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Referee #1

Evidence, reproducibility and clarity

The manuscript by Sequi-Perez explores a somewhat novel role for the transmembrane mucin MUC13 in regulating the tight junction barrier. They report that MUC13 is localized, in part, to the apical junctional complex; that depletion of MUC13 increases TER and expression of claudins and OCLN in a membrane fraction; and that partial removal of MUC13 cytoplasmic domain also results in increased expression of OCLN and claudins, but without a corresponding change in TER. Finally, the authors hypothesize that PKCdelta may act in conjunction with MUC13 to regulate paracellular flux in intestinal epithelial cell lines.

Major points:

1. Although this is an interesting, and generally well-performed study, it is primarily observational and there are few mechanistic insights provided into how MUC13 modulates barrier function. The authors propose a presumably direct interaction between MUC13 and PKC, which apparently sequesters PKC, preventing this kinase from triggering PKC-dependent increases in TJ barrier function; however, there is no evidence that a MUC13-PKC interaction occurs, that MUC13 is phosphorylated by PKC, or that phosphorylation of MUC13 has any impact on its function or overall barrier function. Thus, the hypothesis is not directly tested and all observations in this manuscript are generally correlative in nature. In addition, this model does not explain why all kinase inhibitors tested reverse the increase in TER observed in deltaMUC13 cell lines. Does this reflect the lack of inhibitor specificity or the likelihood that many kinases are involved?
2. The authors do observe that there is an increase in expression of several tight junction-associated proteins, including the claudins, in deltaMUC13 cells. Affected CLDNs include 1, 2, 3, 4, 7, 12. (1) While it appears the authors are arguing that this increased claudin expression results in increased barrier function, they do not sufficiently highlight the well-known role that CLDN2 has in cation transport, and both CLDN-4 and -7 have also been implicated in paracellular ion flux (although this is apparently cell-type specific). These observations would seem to argue against a simple correlation between claudin expression and tight junction barrier function. (2) The increased expression of claudins in the nominally tail-minus MUC13 without a corresponding change in TER would again seem to argue against a simple correlation; (3) Furthermore, the authors should note the disconnect between paracellular ion flux mediated by claudins and the flux of markers such as dextrans and lucifer yellow, which can be dissociated from claudin function.
3. The authors may be overly reliant on TER measurements. Epithelial cells have two parallel resistive pathways: transcellular and paracellular. TER measure the contribution of both. Thus, an increase in TER could result from a decrease in transcellular ion transport. The authors need to measure transcellular ion flow or selectively measure the junctional resistance in a select set of experiments to rule this possibility out.

Minor points:

1. Watch the use of decimal points instead of commas (lines 253 and 256).
2. Consider quantifying all blots (Fig. 5C, Fig. 6B).
3. Line 543: MilliQ is not a washing agent (or is it?).
4. Line 553: TER is the product of total resistance times the area. The units are ohms times area.
5. Line 630: Please provide the transfer conditions (voltage, amp, watts?) and transfer buffer when describing the Western blot protocol.
6. Consider using dot-plots for all quantified data.

Significance

This study advances the fields of mucin biology and tight junction barrier function in an incremental manner. The study is well done, but there are few mechanistic insights into how MUC13 modulates paracellular flux in cultured gut epithelial cells.

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Reply to the reviewers

1. General Statements

We thank all the reviewers for their positive and constructive comments on the manuscript. Changes to the main text have been marked in red text in the uploaded file. We address each of the reviewers’ comments point-by-point below. The major revisions include:

Improved statistical details and attention to subjective language throughout. New TEM data included in the new Figure 1—figure supplement 1 to illustrate the drastic ultrastructural differences between MCs and neighboring epidermal cells. Inclusion of an estimate of the “recombination efficiency” of our keratinocyte lineage trace in Figure 4. Additional quantification of MC density in the different body regions (Figure 6) and prior to squamation (Figure 7F). Imaging of the zebrafish oral mucosa (new Response Figure 1). More nuanced interpretations of the eda and fgf8a mutant phenotypes.

2. Point-by-point description of the revisions

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

The authors describe and characterize the touch system in zebrafish as a new model to study MC development and maintenance. The manuscript is very well written, and the experiments are carefully executed and beautifully illustrated. This study addresses the origin of zebrafish MCs, shows that they are innervated by somatosensory neurons and that they share molecular properties with mammalian MCs. In addition, the authors developed transgenic lines that allow them to study MCs in vivo.

Genetic lineage tracing shows that zf MCs are derived from the epidermis as in mouse and not from neural crest cells, as described for avian MCs. In addition, longevity and turnover of murine MCs was controversial. Here, the authors show that zf MCs constantly turnover and that the distribution and turnover rate in the trunk depends on underlying scales. They show that the loss of scales in eda mutants leads to a decrease in MC production and an increase in MC death showing that scales are required for MC production and maintenance. Using a specific fgf8 mutant allele that causes an increase in Fgf signaling and an increase in scale size they demonstrate that scales are sufficient to induce MCs.

In summary, this manuscript is a rigorous and beautiful characterization of MCs development and maintenance. The authors demonstrate that zebrafish MCs share many characteristics with mammalian MCs. The generation of MCs specific transgenic lines, coupled with existing transgenic lines that label somatosensory cells and cells in the scales sets the stage for detailed further analyses. For example, using these tools one can now study how the size of the MC progenitor domain is controlled, if progenitors migrate and what the identities of the molecular signals from the nerves and scales to progenitors and differentiated MCs are.

Minor comments:

Line 71: Why is the heterogeneity a limitation? Couldn't it also exist in zebrafish?

Thank you for raising this question. The limitations are meant to refer to current limitations of the rodent system and demonstrate an opportunity for a new model system to complement the rodent system. We have rephrased this section to better articulate this point.

Introduction:

“While this system has been useful for understanding many aspects of MC development and function, the rodent system also has several significant limitations that warrant additional models to improve the understanding of MCs.”

We also added the following to the discussion: *“As the majority of the analyses completed here focus on MCs found in the trunk epidermis, it will be intriguing to determine whether all MCs in different skin compartments in the juvenile and adult zebrafish share similar molecular, cellular, and functional properties.” *

Line 295: The authors write: 'Thus, our observations indicate that the decrease in MC cell density in eda mutants is likely due to both reduced MC production and increased MC turnover'.

It should say: '.. increased MC loss'. In mutants the MCs show poor turnover. I believe the term 'turnover' implies that the cells are being replaced, which is only partially happening here.

Thank you for the clarification. We agree with the reviewer and have changed the wording from “turnover” to “loss” in lines 295 and 301.

Line 301: 'The authors state: 'these data suggest that Eda signaling is required for MC development, maintenance, and distribution along the trunk.'

The authors do not show any data that Eda signaling is involved in MC development but only that scales are needed. The MC inducing signals from scales to the epidermis could be independent from Eda signaling. Please rephrase.

Please discuss that not all MC specification/development depends on scales. Even in the scale-less eda mutants some MCs form (as in the inter scale regions in wt?) and even turnover. Do scales secrete a signal that increases proliferation of existing MC progenitors but scales do not affect specification?

We respectfully disagree with the reviewer on the interpretation of these results. Our experimental manipulation (examination of eda-/- vs. sibling controls) only allows us to conclude that Eda signaling - either directly or indirectly - is required for these processes along the trunk. To determine whether signaling from scales is required would require identification of the signal(s) and/or loss/ablation of scales independent of Eda. We have rephrased the results to more clearly state our interpretation. The corresponding portion of the discussion now reads “Further investigations are required to determine whether Eda signaling directly regulates the differentiation of MC progenitors. Alternatively, since eda mutants lack scales (Harris et al., 2008) and have decreased epidermal innervation (Rasmussen et al., 2018), MC development may require scale-derived and/or somatosensory neuron-derived signals.”

Line 320: The authors describe that the fgf8 allele leads to a redistribution of MCs. Is it really a redistribution, or is it ectopic induction or expansion of existing progenitors? Redistribution implies that the expansion is due to a loss of MCs in another region, which I do not see in the data.

Thank you for raising this point about the potentially poor wording choice relating to “redistribution”. We do not yet know whether the distribution of MCs in fgf8a mutants reflects a redistribution, ectopic induction, or expansion of existing progenitors (these are excellent ideas for future studies). Thus, in response to the reviewers comment, we have changed the heading for this results section to “The MC pattern is not predetermined along the trunk” and concluded the section as follows: “... the distribution of MCs tracked with the altered scale size and shape in the mutants, suggesting the MC pattern is not predetermined within the trunk skin compartment (Figure 9E-H).”

Figures:

• Figure 1, panels B-C': EM images are very dark and difficult to see. Letter 'a' is on top of the axon, maybe move to the side and pseudo-color different structures.

In response to these suggestions, we have adjusted the brightness and contrast to lighten the TEM images in Figure 1B-C’ as much as possible. We also moved the ‘a’ off to the side in Figure 1B’ to make the axon more visible. In response to Reviewer #3’s comments (see below), we also added an additional TEM image in the new Figure 1—figure supplement 1 that has presumptive keratinocytes and a MC differentially pseudo-colored. We hesitate to pseudo-color the cells/structures in Figure 1B-C’ for fear of obscuring the underlying TEM images.

• Figure 1, panel D: very difficult to see the magenta axons in the cartoon. Please enlarge and make brighter.

We agree that this needed improvement. In the revised Figure 1D, we made the axons clearer and illustrated the different types of MC-axon associations we observe in Figure 2. We also refer the reader back to this figure in the corresponding axon innervation results section.

• Figure 2, panels A and D: keeping the same antibody stainings in the same color would help with visualization. Matching the bar plots in panel C would be even nicer.

Thank you for the suggestion. The revised Figure 2 now has a consistent color scheme.

• Figure 2, panel C: please identify in the legend if the error bars are SD, SEM or other.

These error bars represent 95% confidence intervals. This information has been added to the figure legend.

• Figure 2, panels G and H: MCs are in cyan in the image, but green in the legend.

This has been corrected.

• Figure 3: include percentages and total number in the image instead of the legend.

The numbers and percentages have now been added to the Figure 3 panels. We have left them in the figure legend for clarity on what was scored.

• Figure 6, panel B: which part of the eye is being depicted?

Thank you for the question. We imaged the corneal epithelium above the lens. This has been clarified in the appropriate parts of Figures 6 and 8 and the corresponding figure legends.

• Figure 6, panel F: please provide error bars and statistics to show that the operculum has a higher density of MCs.

Thank you for the suggestion. In response to the comment, we revised Figure 6F by: 1) increasing the sample size; 2) replotting the data as boxplots rather than bar graphs; and 3) including the results of a one-way ANOVA.

• Figure 7, panels F-H: for simple linear regression, please also provide F and p values.

Thank you for the suggestion. This information has been added to the figure legend.

• Figure 8, panel D: colors for SL do not follow a scale, very hard to understand which is which.

In response to the reviewer’s suggestion, we tried numerous different color palettes. However, we were unable to find a color palette that allowed us to distinguish individual points as well as the rainbow palette used in Figure 8D. Thus, after careful consideration, we have elected to keep the original palette here. For consistency, we have used the same palette in the revised Figure 8–figure supplement 1D and Figure 9–figure supplement 1D.

Methods:

• Line 472: the word "sex" should be used instead of "gender".

Thank you for the correction. This is fixed in the revision.

• Image analysis, line 593. Please provide a more detailed explanation or describe the ImageJ macro used for the analysis.

Our ImageJ macro has been fully annotated and is provided as Figure 2—source code 1 in the revision. The corresponding methods section has also been updated to clarify the methodology.

Reviewer #1 (Significance (Required)):

Soft touch is perceived by Merkel cells (MCs). How MCs develop and are maintained is not well understood because MC development is difficult to study in mammals due to their in utero development. The authors describe and characterize the touch system in zebrafish as a new model to study MC development and maintenance. The study demonstrates that the zebrafish touch system shares many characteristics with its mammalian counterpart, namely its developmental origin, innervation and molecular characteristics. In contrast to mammals, zebrafish transgenic lines that the authors generated, allow the in vivo analysis of Merkel Cell specification, development and maintenance. Therefore this study is the foundation for future detailed cellular and molecular analyses of the touch sensory system and will be of interest to developmental biologists studying stem cells, regeneration and aging, as well as neuroscientists.

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

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

This is a very nice and straightforward paper characterizing mechanosensory Merkel cells in the zebrafish skin. The paper uses a number of criteria, based on our knowledge of Merkel cells in mammals, to identify a population atoh1a expressing cells, with neurosecretory granules and actin rich microvilli as Merkel cells in the zebrafish skin. The authors have used existing transgenic lines and and developed some of their own, described in this paper, to follow the development of Merkel cell in zebrafish. They show that Merkel cells are derived from basal keratinocytes not neural crest cells. They have region specific densities that influenced by underlying structures like scales and fin rays. They go to show that Ectodysplasin signaling promotes Merkel cell development in the trunk skin but not above the eye or operculum. Reduction of Merkel cells in eda mutants suggest that Eda signaling is required for their development and maintenance. Finally they show that alteration of zebfrafish scale pattern using a mutant with exaggerated fgf8a expression also alters merkel cell distribution.

The data presented is clear and the conclusions are supported by their observations.

I have no significant issue with the paper as is.

Reviewer #2 (Significance (Required)):

This study will serve as an excellent basis for future work looking at studies of Merkel cell development and function in fish. Though Merkel cells have been studied in mammals, establishing a zebrafish model for their study will help overcome many barriers that make their analysis difficult in mammals.

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

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

In this manuscript, Brown et al. (2022) seek to characterize and address fundamental questions regarding the development and dynamics of Merkel cells (MCs) in zebrafish (Danio rerio). The authors utilize a diverse and complementary suite of methods to characterize presumptive MCs in the epidermis of adult zebrafish, including electron microscopy, novel transgenic lines, confocal imaging, and various immuno- and non-immunohistological staining techniques. These studies demonstrate that zebrafish MCs share many features with vertebrate (including mammalian) MCs, particularly regarding morphology/structure, putative functions, genetic markers, and bodily distribution.

After establishing the identity of zebrafish MCs, the authors employ lineage tracing and cell tracking analyses to determine that trunk MCs derive from basal keratinocytes and exhibit regular cell turnover. Finally, the authors examine how trunk scales may affect MC development by using established scale mutants. These results show that the presence/absence of scales influences trunk MC development, while scale characteristics (e.g. shape, size) change the distribution of MCs.

MAJOR COMMENTS:

The key conclusions of the manuscript are convincing, however, several points should be addressed by the authors.

Throughout the manuscript, the authors make general claims about zebrafish MCs (zMCs) based on the evidence collected. Yet, most of this evidence (particularly claims about MC turnover, development, structure) comes from examination and experimentation of a specific MC population: trunk MCs located in the scale epidermis. The authors remark upon mammalian MC diversity (lines 73-74) and go on to highlight the diversity of MCs throughout the adult zebrafish (Figure 6), which have differing densities and distribution patterns. Any statements that suggest all zebrafish MCs share certain qualities/features should be carefully considered given the evidence presented.

Thank you for raising this important point. We have added wording in the results and discussion to clearly articulate that the majority of our analyses and conclusions are based on trunk MCs:

Results:

“Anticipating the conclusion of our analysis below, we shall hereafter refer to the epidermal atoh1a+ cells as MCs, with the majority of the analyses completed on trunk MCs unless stated otherwise.”

Discussion:

“As the majority of the analyses completed here focus on MCs found in the trunk epidermis, it will be intriguing to determine whether all MCs in different skin compartments in the juvenile and adult zebrafish share similar molecular, cellular, and functional properties.”

In the manuscript, the authors validate several markers for the identification of zMCs based upon known mammalian markers (e.g. atoh1a, sox2, piezo2, SV2, 5-HT, and AM1-43; Figures 1-3). Yet, another well-known marker for MCs (CK8) is not addressed (Moll, 1995; Moll, 2005). One zebrafish ortholog for CK8 is krt4, a transgene successfully employed in this study to label keratinocytes. Do zMCs express krt4 or other mammalian MC keratins? Answering this question or addressing this discrepancy would further strengthen the authors claims that these cells are bona fide zMCs.

We agree with the reviewer that 1) identification of a keratin(s) that distinguishes MCs from other epidermal cell types in zebrafish would be an excellent reagent; and 2) readers familiar with the mammalian MC literature may similarly wonder why this was not addressed in the manuscript. Indeed, we had considered whether we could identify homologs of CK8, CK20 or other mammalian MC keratins that would label zebrafish MCs. However, despite the confusing nomenclature that would indicate otherwise, the zebrafish keratins share more homology with each other than the corresponding mammalian proteins (Ho et al., 2022; PMID: 34991727). Our revised results section now includes the following to clarify this point: *“For example, keratins, most notably keratin 8 and keratin 20, have been used extensively as markers of mammalian MCs (Moll et al., 1995, 1984). However, zebrafish keratins have undergone extensive gene loss and duplication and are not orthologous to mammalian keratin genes (Ho et al., 2022). Thus, we considered alternative molecular markers to label zebrafish MCs.” *

The authors utilize a previously validated eda mutant line to see if ectodysplasin signaling affects zMC development. While the results of these experiments are convincing, the authors need to make clear whether they are claiming that scales, scale-derived Eda signaling, or Eda signaling alone dictate trunk MC development. It appears that there is some conflation of these ideas, particularly with line 306 ("blocking dermal appendage formation inhibited MC development" is a different claim from 'blocking Eda signaling inhibited MC development'). One way to make this differentiation would be to perform a similar experiment as detailed in Xiao et al. 2016: using a Shh agonist in eda mutants. If scale-specific signals are required in addition to Eda, we would expect to see similar MC densities and patterns in both Shh agonist-treated and non-treated eda mutants.

We agree that our interpretation of these results could have been more clearly articulated in our initial submission. As discussed above in response to Reviewer #1, we do not yet know whether Eda signaling directly or indirectly influences MC development. We have revised the results section to clarify our interpretation of the results as follows: “Together, these data suggest that either Eda signaling, or a scale-derived signal, is required for MC development, maintenance, and distribution along the trunk. Further studies are required to determine the specific scale-derived signal that regulates MC development in the trunk."

The suggestion of using a Shh pathway agonist in eda mutants to attempt to rescue MC differentiation similar to Xiao et al. 2016 is an interesting one. To our knowledge, experiments validating the Smo agonist used by Xiao and colleagues (Hh-Ag1.5) in zebrafish have not been published. We also note that activation of Shh signaling by heat-shock induction of shha expression during squamation led to kyphosis and epidermal migration off of the trunk (Aman et al., 2018; PMID: 30014845). Thus, we respectfully suggest that distinguishing between the various possibilities downstream of Eda is beyond the scope of the current manuscript. We have added a discussion point along these lines: “Further investigations are required to determine whether Eda signaling directly regulates the differentiation of MC progenitors. Alternatively, since eda mutants lack scales (Harris et al., 2008) and have decreased epidermal innervation (Rasmussen et al., 2018), MC development may require scale- and/or somatosensory neuron-derived signals. Finally, we note that trunk MCs are not completely absent in eda mutants, suggesting that a subset of MCs develop independent of Eda signaling.”

Throughout the manuscript, the authors use subjective language (e.g. line 106). While this reviewer does not wish to suppress or alter the authors' voices, careful consideration should be used when employing these types of descriptors. Furthermore, the authors use suggestively quantitative language inappropriately or unjustifiably. For example, in line 221, the authors use "extensive" when describing the co-labeling between atoh1a+ MCs and lineage-traced basal keratinocytes; the percentage of co-labeled cells ranged from 29-32%. Other quantitative descriptors such as "frequently" (line 171) or "uniform" (line 249) describe various features or phenomena without quantification in figures or supplements.

Thank you for this comment. We have paid careful attention to our subjective/statistical language in the revision. Regarding the usage of “uniform” - we have added the wording “relatively uniformly” to descriptions and a statement that our term “uniform” was not specifically quantified. Although the uniform appearance was not specifically quantified, we believe this provides an accurate description of the MC localization pattern in certain skin compartments.

Example word change in Results:

“For example, MCs were distributed relatively uniformly across the eye, although this spatial pattern was not specifically quantified”

In the lineage tracing experiments (Figure 4), the authors note that "recombination is not complete" (lines 1016-1017) to explain why not all zMCs express the basal keratinocyte lineage marker. While this idea could be supported by Figure 4-figure supplement 1, one could postulate that zMCs are derived from multiple progenitor lineages. Using the basal keratinocyte lineage tracing validation, the authors could in theory calculate a "recombination efficiency" of this transgenic line and determine approximately the percent of zMCs they 'lose' as a result. Otherwise, the authors could perform other experiments to support the claim that zMCs derive from basal keratinocytes. For example, could the authors photoconvert basal keratinocytes at 1 dpf and see how many derived MCs are still photoconverted later? Could they do this photoconversion experiment with neural crest cells? Could they ablate neural crest cells and determine if MC number is affected? These additional experiments are not necessarily required for publication, but some explanation of the unexpectedly low percentage of basal keratinocyte lineage marker-labeled MCs would suffice.

We thank the reviewer for raising this important point and the suggestion of calculating a “recombination efficiency”. We note that Cre responsive transgenes are far from a perfect technology in zebrafish as recently characterized by Lalonde et al. (2022; PMID:35582941). In response to the reviewer’s comment, we added an estimate of the recombination efficiency to Figure 4 (panels E, G, H). Importantly, a comparison between the recombination efficiency and percentage of MCs labeled by the basal keratinocyte Cre tracing was not significantly different. Our revised results section reads as follows: “After raising 4-OHT-treated animals to adulthood, we observed variable (2-81%) co-labeling between the basal keratinocyte lineage trace and a MC reporter (Figure 4D’,F). We note that our lineage tracing strategy did not label all basal keratinocytes (Figure 4D; Figure 4—figure supplement 1), suggestive of incomplete Cre-ERT2 induction and/or transgene recombination. Consistent with the latter possibility, a recent analysis demonstrated Tg(actb2:LOXP-BFP-LOXP-DsRed) has a low recombination efficiency compared to other Cre reporter transgenes (Lalonde et al., 2022). To estimate the local recombination efficiency in imaged regions, we thresholded the DsRed channel and calculated the fraction of skin cells labeled (Figure 4E). Importantly, the proportion of MCs labeled by the basal keratinocyte lineage trace was not significantly different from the local recombination efficiency (Figure 4G-H). These observations support a basal keratinocyte origin of most or all zebrafish MCs.”

The authors use appropriate statistics and have sufficient replicates when this information is presented. Yet, the presence or absence of these data is not consistent within figure captions. The authors must ensure that they provide the N of adults and scales (when appropriate), the SL range of adults, and transgenic lines used. Statistics are missing in some figures (for example: Figures 4E, 5D, 5E, 6F, 8S-1E, 9E-H) where it would be appropriate to include them. In some figures, the N changes over time (example: 5D, 5E); an explanation in the 'Methods' section would suffice.

Thank you for noting the need for additional statistics. We have added statistics to the above figures. For Figure 9E-H, we have not added additional statistics. Figure 9E-H serve to graphically visualize differences. We show statistical differences in Figure 9—figure supplement 1 for scale area, aspect ratio, and Feret’s diameter. We have added an explanation related to Figure 5D,E in the methods section: “Animals that died over the course of the experiment were excluded from further analysis.”

MINOR COMMNETS

While the authors present an extensive argument for their claims, addressing these additional comments would further strengthen their story.

Are zMC nuclei lobulated? This ultrastructure characteristic seems to be common in MCs (Chew & Leung, 1994; Tachibana & Nawa, 2002; Moll, 2005; Boulais, 2009).

We have not observed any lobulation of the MC nuclei by TEM, nor was this commented on in the TEM studies of Whitear and colleagues in other teleosts (Lane and Whitear, 1977; PMID: 198137; Whitear, 1989; PMID: 2510796). Nevertheless, we cannot rule out the possibility that serial sectioning or other high resolution analysis of the nuclear shape may reveal such features. In response to the reviewer’s comment, we have added the following paragraph to the discussion: “While our characterization revealed substantial similarities between mammalian and zebrafish MCs, we did observe anatomical differences in line with previous ultrastructural characterizations of teleost MCs (Lane and Whitear, 1977; Whitear, 1989). For example, the nuclei of mammalian MC are commonly lobulated (Boulais et al., 2009; Cheng Chew and Leung, 1994; Moll et al., 2005; Tachibana and Nawa, 2002). While we did not observe lobulation of zebrafish MC nuclei by TEM, we cannot rule out that serial sectioning or high-resolution reconstruction of nuclear shape would reveal lobulation. Mammalian MCs typically localize adjacent to basal keratinocytes (Boot et al., 1992; Cheng Chew and Leung, 1994; Fradette et al., 1995; Mihara et al., 1979; Moll et al., 1996; Smith, Jr, 1977), whereas zebrafish MCs appear in upper strata, typically beneath the periderm (Figure 1D,G’’). As the majority of the analyses completed here focus on MCs found in the trunk epidermis, it will be intriguing to determine whether all MCs in different skin compartments in the juvenile and adult zebrafish share similar properties.”

In Figure 3C and 3", the authors show that AM1-43 labels zMCs. Yet, this technique should also stain sensory axons that associate with MCs (Meyers, 2003). Are axons also stained? Other positive controls for the stains could be useful as a supplement.

The reviewer is correct that Meyers et al., (2003; PMID: 12764092) report AM1-43 staining of neurites that innervate MCs in the whisker follicle. However, they did not report similar staining of neurites innervating touch dome MCs. In murine hairy skin, the related styryl dye FM1-43 appears to most prominently stain MCs and hair follicle-associated lanceolate endings (Banks et al., 2013 PMID: 23440964; Villarino et al., 2022 preprint DOI: 10.1101/2022.05.26.493600). Our revised legend for Figure 3 now includes the following: “AM1-43 has been reported to stain neurites innervating MCs in murine whisker vibrissae (Meyers et al., 2003). However, our AM1-43 staining regiment did not strongly label cutaneous axons, although we cannot exclude low levels of staining.”

All of the stains used in our original Figure 3 have been previously validated in zebrafish, which we have more clearly stated and cited in the corresponding results section of the revision. Because these reagents have all been previously validated and our staining patterns are consistent with the literature, we respectfully suggest that positive controls would add little value to the current manuscript. Nevertheless, in response to the reviewer’s comment, we confirmed our piezo2 FISH staining using an independent method (a piezo2 HCR probe). We have included these HCR results as the updated Figure 3D and moved the original Figure 3D to Figure 3—figure supplement 1.

In Figure 7, the authors argue that as scales develop, MC density increases with scale area. Did the authors compare MC densities of differently-sized scales at the same age? Is fish SL/age a potential confound in the interpretation of these data?

Thank you for the suggestion. In response to the reviewer’s comment, we have replotted the data in Figure 7G,H for animals in the range 8-10 mm SL in Figure 7—figure supplement 1. We have revised the corresponding results section as follows: “The density and number of MCs positively correlated with scale area (Figure 7G,H), although this trend was less pronounced at stages less than 10 mm (Figure 7—figure supplement 1)”. As discussed above in response to reviewer #1’s suggestion, we also now report F-statistics and P-values for the linear regressions in the figure legends.

The authors claim that squamation begins at ~9 mm SL (line 268), prior to which MCs were "rare" in the epidermis (supported by data in Figure 7F). However, Figures 8A and 8G suggest that MCs are not rare prior to squamation/9 mm SL. Are these data in conflict?

Thank you for raising this observation. We do not believe these data are in conflict. Figure 8A and B show images of fish 8.8-8.9 mm SL, immediately prior to squamation. MCs appear about the same time as scales develop but the exact timing varies between animals. To further strengthen this section of the manuscript, we now include quantification of the density of trunk MCs at various stages prior to 9 mm SL (new data added to the developmental timeline in Figure 7F). These data are consistent with our initial interpretation. In the revised results section we clarify this as follows: “Using reporters that label MCs and scale-forming osteoblasts, we rarely observed MCs in the epidermis prior to 8 mm SL (Figure 7B, F). Between 8-10 mm SL, MCs appeared at a low density along the trunk (Figure 7F). MC density rapidly increased from 10-15 mm SL, a period of active scale growth (Figure 7C-F).”

In Figure 6B-E, the panels are incorrectly labeled as "atoh1a:nls-Eos" (figure caption and fluorescence localization show they are atoh1a:Lifeact-EGFP).

The low magnification panels were correctly labeled as atoh1a:nls-Eos. The insets showed atoh1a:Lifeact-EGFP as described in the figure legend. We apologize for the confusion and poor data presentation. We have revised Figure 6 to eliminate the problematic labeling/display.

Figure 9 panels E-H are not referenced in the main body of the text.

Thank you for pointing this out. Fixed in the revised manuscript.

In Figure 6, the authors examine MC densities in the tail, but do not quantify changes here with eda mutants as they did for other regions (eye, operculum) in Figure 8. Why was this region not examined?

We have clarified this point in the revised results section as follows: “eda mutants lack fins at the stages analyzed (Harris et al., 2008) precluding analysis of these regions in the homozygous mutants.”

The authors do a good job in detailing the current literature regarding MCs, however, two missing areas are noticeable: 1) there is no mention of mammalian MCs that reside in the oral mucosa (Hashimoto, 1972) or whether they exist in zebrafish, and 2) no mention of Merkel-like cells (Halata, 2003) and why the cells in this paper are or are likely not Merkel-like cells.

Thank you for the suggestions. Regarding the first point, we revised the introduction to reference (Hashimoto, 1972) as follows: “...vertebrates have diverse types of skin and MCs are found in both hairy and glabrous (non-hairy) skin, as well as mucocutaneous regions such as the gingiva and palate (Hashimoto, 1972; Lacour et al., 1991; Moayedi et al., 2021).” We also imaged the mucosal tissue along the roof palate of the adult mouth and identified atoh1a+ cells (see Response Figure 1 below). Close examination of the atoh1a:Lifeact-EGFP signal revealed these cells have a spherical morphology and extend short processes similar to the MCs described across the body regions examined in Figure 6. However, as the microvillar morphology of the palatal atoh1a+ cells is not identical to those identified in other skin regions, we hesitate to call these MCs without performing additional in-depth analyses. We feel that inclusion of these data in the manuscript could distract the reader from the main focus of our study, therefore we have included them here:

__Response Figure 1. atoh1a+ cells in the adult oral epithelium. (A,B) __Low- (A) and high-magnification (B) confocal micrographs of oral roof palate epithelium in an adult expressing reporters for keratinocytes (Tg(krt4:DsRed)) and atoh1a-expressing cells (Tg(atoh1a:Lifeact-EGFP)). (B’) Reconstructed cross section along the yellow line in B showing two atoh1a+ cells in the upper strata of the oral epithelium. Scale bars: 50 µm (A) and 10 µm (B,B’).

Regarding the second point, we have added the following sentence to the first paragraph of the discussion: “Second, zebrafish MCs extend numerous short, actin-rich microvilli and complex with somatosensory axons, classic morphological hallmarks of MCs (Mihara et al., 1979; Smith, Jr, 1977; Toyoshima et al., 1998). Our morphological observations support the interpretation that these cells are MCs rather than Merkel-like cells, which lack axon association and microvillar processes (reviewed by Halata et al., 2003).”

It may help readers understand MC morphology in context if the authors include a larger picture of the TEM data that highlights the drastic difference in ultrastructure between MCs and neighboring keratinocytes.

Thank you for the suggestion. We added a new figure (Figure 1—figure supplement 1) to the revised manuscript that contains an additional TEM image that we believe illustrates the different morphologies of keratinocytes and MCs. We hope this will help the reader contextualize the morphology and position of MCs within the zebrafish epidermis. This is now referenced in the first results section as follows: “The cells appeared relatively small and spherical with a low cytoplasmic-to-nuclear ratio compared to neighboring keratinocytes (Figure 1B,C; Figure 1—figure supplement 1) …”

Reviewer #3 (Significance (Required)):

The current manuscript provides significant advancements in various biological fields and research communities. For researchers that utilize zebrafish as a model organism, these findings present a new cell type along with novel and essential genetic tools for study. These developments open the possibilities to further understand MCs, their roles in somatosensory function, mechanisms of cell type diversification, and to engage in translational research. For those already researching MCs, this manuscript shows that fundamental questions regarding MC functioning can be rigorously addressed with a new model that can fill the methodological limitations imposed by mammalian biology. Indeed, the authors do a thorough job of introducing and contextualizing our knowledge of MCs and any outstanding gaps. The authors then sit their findings comfortably alongside previous works, largely supporting those findings, and take the extra step to address MC controversies/matters of debate. This technique of supporting the current literature and then uplifting it with new findings makes this work even more impressive. Various audiences will find value in this manuscript, including but not limited to those that study epidermal cell types, the development and influence of skin appendages, somatosensation and sensory disorders, developmental biology, and Merkel cell carcinoma.

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

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, Brown et al. (2022) seek to characterize and address fundamental questions regarding the development and dynamics of Merkel cells (MCs) in zebrafish (Danio rerio). The authors utilize a diverse and complementary suite of methods to characterize presumptive MCs in the epidermis of adult zebrafish, including electron microscopy, novel transgenic lines, confocal imaging, and various immuno- and non-immunohistological staining techniques. These studies demonstrate that zebrafish MCs share many features with vertebrate (including mammalian) MCs, particularly regarding morphology/structure, putative functions, genetic markers, and bodily distribution.

After establishing the identity of zebrafish MCs, the authors employ lineage tracing and cell tracking analyses to determine that trunk MCs derive from basal keratinocytes and exhibit regular cell turnover. Finally, the authors examine how trunk scales may affect MC development by using established scale mutants. These results show that the presence/absence of scales influences trunk MC development, while scale characteristics (e.g. shape, size) change the distribution of MCs.

MAJOR COMMENTS:

The key conclusions of the manuscript are convincing, however, several points should be addressed by the authors.

• Throughout the manuscript, the authors make general claims about zebrafish MCs (zMCs) based on the evidence collected. Yet, most of this evidence (particularly claims about MC turnover, development, structure) comes from examination and experimentation of a specific MC population: trunk MCs located in the scale epidermis. The authors remark upon mammalian MC diversity (lines 73-74) and go on to highlight the diversity of MCs throughout the adult zebrafish (Figure 6), which have differing densities and distribution patterns. Any statements that suggest all zebrafish MCs share certain qualities/features should be carefully considered given the evidence presented.

• In the manuscript, the authors validate several markers for the identification of zMCs based upon known mammalian markers (e.g. atoh1a, sox2, piezo2, SV2, 5-HT, and AM1-43; Figures 1-3). Yet, another well-known marker for MCs (CK8) is not addressed (Moll, 1995; Moll, 2005). One zebrafish ortholog for CK8 is krt4, a transgene successfully employed in this study to label keratinocytes. Do zMCs express krt4 or other mammalian MC keratins? Answering this question or addressing this discrepancy would further strengthen the authors claims that these cells are bona fide zMCs.

• The authors utilize a previously validated eda mutant line to see if ectodysplasin signaling affects zMC development. While the results of these experiments are convincing, the authors need to make clear whether they are claiming that scales, scale-derived Eda signaling, or Eda signaling alone dictate trunk MC development. It appears that there is some conflation of these ideas, particularly with line 306 ("blocking dermal appendage formation inhibited MC development" is a different claim from 'blocking Eda signaling inhibited MC development'). One way to make this differentiation would be to perform a similar experiment as detailed in Xiao et al. 2016: using a Shh agonist in eda mutants. If scale-specific signals are required in addition to Eda, we would expect to see similar MC densities and patterns in both Shh agonist-treated and non-treated eda mutants.

• Throughout the manuscript, the authors use subjective language (e.g. line 106). While this reviewer does not wish to suppress or alter the authors' voices, careful consideration should be used when employing these types of descriptors. Furthermore, the authors use suggestively quantitative language inappropriately or unjustifiably. For example, in line 221, the authors use "extensive" when describing the co-labeling between atoh1a+ MCs and lineage-traced basal keratinocytes; the percentage of co-labeled cells ranged from 29-32%. Other quantitative descriptors such as "frequently" (line 171) or "uniform" (line 249) describe various features or phenomena without quantification in figures or supplements.

• In the lineage tracing experiments (Figure 4), the authors note that "recombination is not complete" (lines 1016-1017) to explain why not all zMCs express the basal keratinocyte lineage marker. While this idea could be supported by Figure 4-figure supplement 1, one could postulate that zMCs are derived from multiple progenitor lineages. Using the basal keratinocyte lineage tracing validation, the authors could in theory calculate a "recombination efficiency" of this transgenic line and determine approximately the percent of zMCs they 'lose' as a result. Otherwise, the authors could perform other experiments to support the claim that zMCs derive from basal keratinocytes. For example, could the authors photoconvert basal keratinocytes at 1 dpf and see how many derived MCs are still photoconverted later? Could they do this photoconversion experiment with neural crest cells? Could they ablate neural crest cells and determine if MC number is affected? These additional experiments are not necessarily required for publication, but some explanation of the unexpectedly low percentage of basal keratinocyte lineage marker-labeled MCs would suffice.

• The authors use appropriate statistics and have sufficient replicates when this information is presented. Yet, the presence or absence of these data is not consistent within figure captions. The authors must ensure that they provide the N of adults and scales (when appropriate), the SL range of adults, and transgenic lines used. Statistics are missing in some figures (for example: Figures 4E, 5D, 5E, 6F, 8S-1E, 9E-H) where it would be appropriate to include them. In some figures, the N changes over time (example: 5D, 5E); an explanation in the 'Methods' section would suffice.

MINOR COMMENTS:

While the authors present an extensive argument for their claims, addressing these additional comments would further strengthen their story.

• Are zMC nuclei lobulated? This ultrastructure characteristic seems to be common in MCs (Chew & Leung, 1994; Tachibana & Nawa, 2002; Moll, 2005; Boulais, 2009).

• In Figure 3C and 3", the authors show that AM1-43 labels zMCs. Yet, this technique should also stain sensory axons that associate with MCs (Meyers, 2003). Are axons also stained? Other positive controls for the stains could be useful as a supplement.

• In Figure 7, the authors argue that as scales develop, MC density increases with scale area. Did the authors compare MC densities of differently-sized scales at the same age? Is fish SL/age a potential confound in the interpretation of these data?

• The authors claim that squamation begins at ~9 mm SL (line 268), prior to which MCs were "rare" in the epidermis (supported by data in Figure 7F). However, Figures 8A and 8G suggest that MCs are not rare prior to squamation/9 mm SL. Are these data in conflict?

• In Figure 6B-E, the panels are incorrectly labeled as "atoh1a:nls-Eos" (figure caption and fluorescence localization show they are atoh1a:Lifeact-EGFP).

• Figure 9 panels E-H are not referenced in the main body of the text.

• In Figure 6, the authors examine MC densities in the tail, but do not quantify changes here with eda mutants as they did for other regions (eye, operculum) in Figure 8. Why was this region not examined?

• The authors do a good job in detailing the current literature regarding MCs, however, two missing areas are noticeable:

1) there is no mention of mammalian MCs that reside in the oral mucosa (Hashimoto, 1972) or whether they exist in zebrafish, and

2) no mention of Merkel-like cells (Halata, 2003) and why the cells in this paper are or are likely not Merkel-like cells.

• It may help readers understand MC morphology in context if the authors include a larger picture of the TEM data that highlights the drastic difference in ultrastructure between MCs and neighboring keratinocytes.

Significance

The current manuscript provides significant advancements in various biological fields and research communities. For researchers that utilize zebrafish as a model organism, these findings present a new cell type along with novel and essential genetic tools for study. These developments open the possibilities to further understand MCs, their roles in somatosensory function, mechanisms of cell type diversification, and to engage in translational research. For those already researching MCs, this manuscript shows that fundamental questions regarding MC functioning can be rigorously addressed with a new model that can fill the methodological limitations imposed by mammalian biology. Indeed, the authors do a thorough job of introducing and contextualizing our knowledge of MCs and any outstanding gaps. The authors then sit their findings comfortably alongside previous works, largely supporting those findings, and take the extra step to address MC controversies/matters of debate. This technique of supporting the current literature and then uplifting it with new findings makes this work even more impressive. Various audiences will find value in this manuscript, including but not limited to those that study epidermal cell types, the development and influence of skin appendages, somatosensation and sensory disorders, developmental biology, and Merkel cell carcinoma.

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Referee #2

Evidence, reproducibility and clarity

This is a very nice and straightforward paper characterizing mechanosensory Merkel cells in the zebrafish skin. The paper uses a number of criteria, based on our knowledge of Merkel cells in mammals, to identify a population atoh1a expressing cells, with neurosecretory granules and actin rich microvilli as Merkel cells in the zebrafish skin. The authors have used existing transgenic lines and and developed some of their own, described in this paper, to follow the development of Merkel cell in zebrafish. They show that Merkel cells are derived from basal keratinocytes not neural crest cells. They have region specific densities that influenced by underlying structures like scales and fin rays. They go to show that Ectodysplasin signaling promotes Merkel cell development in the trunk skin but not above the eye or operculum. Reduction of Merkel cells in eda mutants suggest that Eda signaling is required for their development and maintenance. Finally they show that alteration of zebfrafish scale pattern using a mutant with exaggerated fgf8a expression also alters merkel cell distribution.

The data presented is clear and the conclusions are supported by their observations.

I have no significant issue with the paper as is.

Significance

This study will serve as an excellent basis for future work looking at studies of Merkel cell development and function in fish. Though Merkel cells have been studied in mammals, establishing a zebrafish model for their study will help overcome many barriers that make their analysis difficult in mammals.

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Referee #1

Evidence, reproducibility and clarity

The authors describe and characterize the touch system in zebrafish as a new model to study MC development and maintenance. The manuscript is very well written, and the experiments are carefully executed and beautifully illustrated. This study addresses the origin of zebrafish MCs, shows that they are innervated by somatosensory neurons and that they share molecular properties with mammalian MCs. In addition, the authors developed transgenic lines that allow them to study MCs in vivo.

Genetic lineage tracing shows that zf MCs are derived from the epidermis as in mouse and not from neural crest cells, as described for avian MCs. In addition, longevity and turnover of murine MCs was controversial. Here, the authors show that zf MCs constantly turnover and that the distribution and turnover rate in the trunk depends on underlying scales. They show that the loss of scales in eda mutants leads to a decrease in MC production and an increase in MC death showing that scales are required for MC production and maintenance. Using a specific fgf8 mutant allele that causes an increase in Fgf signaling and an increase in scale size they demonstrate that scales are sufficient to induce MCs.

In summary, this manuscript is a rigorous and beautiful characterization of MCs development and maintenance. The authors demonstrate that zebrafish MCs share many characteristics with mammalian MCs. The generation of MCs specific transgenic lines, coupled with existing transgenic lines that label somatosensory cells and cells in the scales sets the stage for detailed further analyses. For example, using these tools one can now study how the size of the MC progenitor domain is controlled, if progenitors migrate and what the identities of the molecular signals from the nerves and scales to progenitors and differentiated MCs are.

Minor comments:

Line 71: Why is the heterogeneity a limitation? Couldn't it also exist in zebrafish? Line 295: The authors write: 'Thus, our observations indicate that the decrease in MC cell density in eda mutants is likely due to both reduced MC production and increased MC turnover'. It should say: '.. increased MC loss'. In mutants the MCs show poor turnover. I believe the term 'turnover' implies that the cells are being replaced, which is only partially happening here. Line 301: 'The authors state: 'these data suggest that Eda signaling is required for MC development, maintenance, and distribution along the trunk.' The authors do not show any data that Eda signaling is involved in MC development but only that scales are needed. The MC inducing signals from scales to the epidermis could be independent from Eda signaling. Please rephrase. Please discuss that not all MC specification/development depends on scales. Even in the scale-less eda mutants some MCs form (as in the inter scale regions in wt?) and even turnover. Do scales secrete a signal that increases proliferation of existing MC progenitors but scales do not affect specification? Line 320: The authors describe that the fgf8 allele leads to a redistribution of MCs. Is it really a redistribution, or is it ectopic induction or expansion of existing progenitors? Redistribution implies that the expansion is due to a loss of MCs in another region, which I do not see in the data.

Figures:

• Figure 1, panels B-C': EM images are very dark and difficult to see. Letter 'a' is on top of the axon, maybe move to the side and pseudo-color different structures.

• Figure 1, panel D: very difficult to see the magenta axons in the cartoon. Please enlarge and make brighter.

• Figure 2, panels A and D: keeping the same antibody stainings in the same color would help with visualization. Matching the bar plots in panel C would be even nicer.

• Figure 2, panel C: please identify in the legend if the error bars are SD, SEM or other.

• Figure 2, panels G and H: MCs are in cyan in the image, but green in the legend.

• Figure 3: include percentages and total number in the image instead of the legend.

• Figure 6, panel B: which part of the eye is being depicted?

• Figure 6, panel F: please provide error bars and statistics to show that the operculum has a higher density of MCs.

• Figure 7, panels F-H: for simple linear regression, please also provide F and p values.

• Figure 8, panel D: colors for SL do not follow a scale, very hard to understand which is which.

Methods:

• Line 472: the word "sex" should be used instead of "gender".

• Image analysis, line 593. Please provide a more detailed explanation or describe the ImageJ macro used for the analysis.

Significance

Soft touch is perceived by Merkel cells (MCs). How MCs develop and are maintained is not well understood because MC development is difficult to study in mammals due to their in utero development. The authors describe and characterize the touch system in zebrafish as a new model to study MC development and maintenance. The study demonstrates that the zebrafish touch system shares many characteristics with its mammalian counterpart, namely its developmental origin, innervation and molecular characteristics. In contrast to mammals, zebrafish transgenic lines that the authors generated, allow the in vivo analysis of Merkel Cell specification, development and maintenance. Therefore this study is the foundation for future detailed cellular and molecular analyses of the touch sensory system and will be of interest to developmental biologists studying stem cells, regeneration and aging, as well as neuroscientists.

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Reply to the reviewers

Official Revision Plan Document:

Manuscript number: #RC-2022-01681

Corresponding author(s): Nicholas, Leigh

1. General Statements

We sincerely appreciate these positive and helpful reviews. We are grateful for the constructive comments and we outline our responses below. Addressing these comments will further broaden the impact of the work and increase the power, reliability, and application of single cell approaches while decreasing the cost and labor intensive collection steps.

As single cell sequencing approaches have entered the mainstream, we are still finding flaws and artifacts from these methods. A major limitation of widely used collection approaches is a difficulty in obtaining biological replicates, which are required to generate robust sequencing datasets. In general, a lack of biological replicates has been a major oversight in the vast majority of single cell studies, and any technique that can facilitate biological replicate collection should be widely applied. The elegance of SNP-based demultiplexing lies in the fact that it can be applied regardless of any external label, applied to previously collected data, and the data are already collected for every sample sequenced. We were pleased to have the reviewers agree and identify the many conceptual advances in this manuscript, with one major critique being noted by one reviewer as a lack of novelty.

Regarding the lack of novelty, we appreciate that SNP-based demultiplexing was not developed as a method within this manuscript, but disagree that a broad benchmarking and validation study that opens the doors to the use of SNP-based demuxing in any species with sufficient between animal genetic heterogeneity lacks novelty. To address this concern, we will now further emphasize the drawbacks and artifacts that can arise in the currently common practice of pooling samples and choosing not to demultiplex, while improving our explanation of our discoveries in this manuscript. The lack of biological replicates in single cell sequencing studies is rampant and needs to be addressed with approaches such as those demonstrated here. We also want to emphasize the importance of validating and benchmarking bioinformatic approaches with orthogonal, priorly established approaches (eg. wet-lab based methods), which had previously not been conducted for SNP-based demultiplexing, outside of human samples. The inbred nature of common lab animals and broad range in quality and availability of genomic resources make this a major step forward in bringing SNP-demultiplexing to all labs. We believe that our paper broadly extends, benchmarks and most importantly validates the advantages and limitations of SNP-based demuxing across various species.

2. Description of the planned revisions

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

“Cardiello et al tested if souporcell (https://pubmed.ncbi.nlm.nih.gov/32366989/) can be used to demultiplex samples for some model organisms, based on identified SNPs. For this, they used synthetic multiplexed data, publicly available datasets and some new datasets, spanning samples from five model organisms. Their analysis indicates that souporcell could be used to

demultiplex scRNA-seq experiments for multiple species, which offers a cost-beneficent approach.

The manuscript reads well and shows this approach can work for different model organisms. However, unfortunately, I am confused about the amount of novelty in this manuscript. The method, souporcell, is already published. The authors indicate souporcell is not validated in non-human samples, but the original paper states that their method works with malaria parasite data (Fig 3b, FigS4). Adapting and using an available tool for different model organisms is good and groups working on different model organisms may find this manuscript useful, but the same could be said for the original article. Due to these reasons, I am not sure whether this manuscript has novelty sufficient for publication.”

__Our response: __We appreciate this constructive criticism that helped us realize that our novelty was not clearly stated in the first version of the manuscript. We need to improve our Introduction and our verbiage as to what has been previously performed and how this current manuscript provides novel insight into multiple previously unanswered questions which broadly extend the utility of SNP-based demultiplexing. To address this comment, we will revamp our Introduction, Results, and Discussion to more clearly highlight the novelty of this work.

Planned revisions:

Defining “validation”. We define validation as establishing the accuracy or validity of a method. Therefore, validation of SNP-based demultiplexing for use in non-human species requires comparison to an already proven, orthogonal method, such as a wet-lab based demultiplexing approach. The souporcell paper does not validate (i.e., confirm with an orthogonal wet-lab method) the results from souporcell in any species but humans. This lack of validation for SNP-based demultiplexing in samples from non-human species made it unclear how and if these approaches would work in other species. Human samples are expected to perform exceptionally well in this approach due to their extremely high genetic diversity and wealth of available genomic resources. Thus, while it was exciting that the original souporcell authors chose to try applying their algorithm to a non-human (e.g., malarial parasite) dataset, the paper left many unanswered questions about potential uses and accuracy. In addition to validating the accuracy of souporcell results in many species, we demonstrated that souporcell shows a relatively poor ability to call doublets in many non-human vertebrates. In addition to highlighting a novel drawback of the method, this demonstrates the need to validate the accuracy of different aspects of tools like souporcell when applied to new systems rather than use souporcell or other SNP-demuxers prior to validation. Highlighting other novel findings in this work: For instance, our assessment of which genomic resources are required for using SNP-based demultiplexing in different species, whether this could be applied to lab animals likely to be inbred to various degrees (and to address other reviewers comments, the inbred level permitted), assessment of the accuracy of SNP-demultiplexing in species with alignment references of varying qualities (i.e., only de novo transcriptome) and genomes of varying sizes (up to 30Gb, 10 times larger that of human, which can be extremely computational intensive), and the exploration of pooling and demultiplexing of multiple species in a single library. Making clear how we made the necessary adjustments to the original souporcell pipeline to successfully apply it to datasets with various resources available in these species.

(Reviewer #1): I also wrote down two minor points below:

“1- Doublets assigned by souporcell compared to the fluor-based assignment look random. In Fig 2 doublet recovery rate looks smaller, and in fig 3 doublet rate prediction looks more random. This is a bit confusing. Is there any explanation for this?”

__Our response: __We agree and thus noted in the manuscript that the detection of doublets in these datasets by Souporcell are not very reliable.

Planned revisions:

We will expand our Discussion to include brief hypotheses for factors that likely contributed to poor doublet detection by souporcell in these analyses. In the Discussion we will clearly suggest complementary approaches for improving the detection/removal of doublets in pooled scRNA-seq experiments through applying external gene expression-based doublet detection programs. We will also attempt to use these programs on at least one of our datasets to see how well independant doublet detection methods complement souporcell on pooled datasets. A full benchmarking of these doublet detection methods already exists and will be referenced in our Discussion.

Reviewer #1: “2- The authors discussed the immune system cells might show some variability in their discussion (referring to fig 3), but this is not clearly shown in the figures as data. Having a percentage bar graph could make it clearer for the readers.”

__Our response: __This is a valid point that we plan to address with the addition of a new figure as well as some clarifications in the text.

Planned revisions:

We will make a supplemental figure for Figure 3 in which we clearly demonstrate animal to animal variability. (bar plot of absolute cell numbers present from each individual animal present in each cell cluster as requested). In the new supplemental figure we will also include a new UMAP plot of fluorescently assigned cell identities belonging only to one of the three animals, which makes it easier to visualize the difference in numbers of cells from each animal present in each individual cell cluster. We will also cite papers that have already demonstrated the phenomena of animal to animal variability in scRNA-seq datasets. We will further emphasize that even in the absence of animal-to-animal variability in co-clustering, that demultiplexing pooled datasets is important because differential expression analysis is greatly enhanced with biological replicates.

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

Major comments:

“1. SNP-based demultiplexing performed well on some species, such as zebrafish and Africa green monkey, from which over 90% of the cells analyzed were correctly identified. However, this accuracy decreases in Pleurodeles samples when a common SNPs VCF file is absent (Fig.3). It showed that cell identity can be more precisely defined with the increase of average read depth (Fig 3B). So, I am wondering whether the mis-defined cells shown in Fig. 3E, actually are cells with lower reads. It is better if the authors can test such a correlation between the cell identity and the depth of reads using the data from Fig. 3E.”

__Our response: __We are thankful to reviewer #2 for raising such a great point. We do see the accuracy of the benchmarking results for this experiment increase with increasing sequence depth/cell quality. However, the reasons for this are potentially more complex than just higher accuracy of souporcell in higher quality cells: The fluorescent-based demultiplexing that is being used for “ground truth” in benchmarking souporcell for this figure is more accurate in cells with higher read depth because more fluorescent gene reads are likely to be captured. Therefore analyzing the accuracy of souporcell relative to fluorescent-based demultiplexing over varying read depths can be confusing because it is possible that both methods improve in accuracy with higher read depth. Figure 3B attempts to illustrate this concept, and to demonstrate why we chose to benchmark only the cells with sufficient read depth (read depth between 5K, and 40K, and >1 fluorescent gene read per cell). We plan to complement our manuscript with additional figures and text that will make this clearer.

Planned revisions:

We will produce a plot similar to Figure 3B, but with a Y axis that is the percent agreement between the two methods. For Figure 4 we will also make a plot showing percent agreement between demux methods versus read depth. This plot will be a useful comparison to investigate whether scRNA read depth is directly affecting the quality of souporcell’s SNP-based demux results. Plotting this comparison for a dataset in which Cellplex/Cell hashing is the benchmarking demux method is a more fair test of the effect of sequencing depth on the souporcell demux results because cellplex results rely on reads from the cellplex library, which are an independent sequencing library from the scRNA reads. We will investigate whether the use of a common VCF file or lack thereof affects souporcell accuracy. To test this, we will try repeating souporcell demux of one dataset with and without a common VCF file input to see if the VCF file inclusion affects the accuracy of souporcell results.

Reviewer #2:

“2. Please discuss limitations of this approach in the manuscript. (1) To which extent, when SNPs are roughly present in the individuals of same species, SNP-based demultiplexing can be applied, e.g., individuals from an inbred strain (c57bl6 mice) would not work.(2) The authors experimentally tested two newt species using SNP-based demultiplexing. When multiple species are experimentally applied, may the cell/nuclei size variation cause problem?”

__Our response: __We agree with Reviewer 2 that this paper brings up many technical questions about the limits to which SNP-based demultiplexing will succeed. These limitations should be addressed more thoroughly in our Discussion section.

Planned revisions:

We will expand our Discussion to more fully discuss the predicted limits for SNP-based demuxing for separating pooled cells from genetically similar individuals. We referenced the single paper previously published which reported that Freemuxlet, a similar approach to souporcell, did not succeed when applied to cells pooled from multiple animals within an inbred mouse strain, but did succeed across mouse strains (though without any validation of results). We will expand this Discussion to address the expected effects of genetic diversity on the success of SNP-based demultiplexing methods. We will also note in this expanded Discussion that SNP-based demuxing worked in this paper on siblings (some of the xenopus, some of the zebrafish), and other SNP-based demuxers have been used successfully for demuxing cells from closely related individuals including human siblings (scSplit) and human maternal/fetal pairs (souporcell). We will expand our Discussion to address the potential drawbacks of pooling cells from different species or tissue types including the possibility of a bias in scRNA-seq sample preparation methods. We expect that variations in cell or nuclei sizes between species could cause biases in cell capture depending on the scRNA-seq library preparation method, especially with microfluidic based scRNA-seq preparation methods. We will search for a dataset that would allow for synthetic pooling of inbred mouse data and, if available, put this through our synthetic pooling and demuxing pipeline. While other papers have reported this does not work with other SNP demux tools, and on comments on the souporcell github (https://github.com/wheaton5/souporcell/issues/154) it does not seem to be working, we feel this would be a nice test/reference for showing the limitations for SNP-based demuxing in highly genetically similar individuals.

(Reviewer #2)* *

“3. What is the upper limit number of samples when using this model. Please make some estimation or discussion about it.”

__Our response: __We think this is a pressing question for the future of SNP-based demuxing and deserves further discussion in this manuscript. This is directly addressed by the authors of souporcell in a github thread with regard to human samples (worked on 21 human samples, may work in up to 40). At this point, we have no reason to believe that the limit on sample numbers should be different in other species.

Planned revisions:

We will include discussion about potential limits for the maximum number of samples that can be pooled and demuxed using this approach. As discussed below in response to reviewer 3, we will quantify the genetic differences in pooled datasets in this manuscript in order to give readers an improved prediction of how well SNP-based demuxers are likely to work on their animals of interest. We will look for previously published pooled dataset from zebrafish that includes multiple dozens of samples and attempt to SNP-demultiplex this pool. While we will be unable to validate the accuracy, given how well SNP-based demuxing has performed we can at least determine if cell origins are assigned.

Reviewer #2: Minor comments:

“1. Please add an algorithm principle of this model.”

__Our response: __Thanks for the suggestion, we will do so.

Planned revision:

We will direct readers to the algorithm principle of souporcell in the original paper and include a flowchart of our workflow for running souporcell piece by piece as we have done in the manuscript. As mentioned above, we will make clear how we made the necessary adjustments to the original souporcell pipeline to successfully apply it to datasets with various resources available in these species.

Reviewer #2:

“2. Give a clear definition of doublets including the ground truth and Souporcell result.”

__Our response: __We appreciate this recommendation. For the purposes of this paper our definition of a ‘doublet’ is a dataset represented by a single cell barcode that actually contains more than one cell. However, true doublets can be identified with absolute certainty only in our synthetically pooled datasets, because no demultiplexing approach used for benchmarking is 100% accurate. Therefore, ‘true doublet’ will refer to known doublets based on synthetically pooled dataset ground truths. Further, for our experimental datasets we will also use ‘confirmed doublet’ to refer to cells that were called doublets by both the ground truth and souporcell. And we will use ‘contested doublet’ to refer to cells in which the experimentally derived ground truth and souporcell result disagree about a potential doublet.

Planned revision:

We will insert a clear definition of doublets used in this paper as described above, including the complexity in identifying which doublets are real given the relationship between ground truth and the souporcell results for each experiment.

Reviewer #2:

“3. Authors should indicate the time cost of running one round of such analysis, the minimal computational requirements?”

__Our response: __This is an important point and will be helpful to readers.

Planned revision:

We will add to the manuscript information on the required time, RAM consumption, and computational requirements for running various setups for souporcell.

Reviewer #3: Major comments:

“The manuscript makes a convincing case for the ability of a preexisting SNP-based demultiplexing tool, called souporcell, to demultiplex pooled samples. The study uses three methods for validation: 1. In silico data pooling; 2. Pooling of transgenic lines; 3. Pooling of cells tagged with CMOs (10x genomics). The results are consistent across experiments.

The authors propose that souporcell is a solution for demultiplexing pooled samples whenever sample tagging methods are not feasible. Although the authors test this approach in several species and conditions, the validation does not cover all possible cases and situations, obviously. Indeed, the authors recommend potential users to run pilot validation experiments with a secondary demultiplexing methods.

However, the manuscript would become more useful if the following points are addressed:

First, what is the genetic relatedness of the individuals pooled in the experiments? What is the SNP frequency in the samples analyzed, and how does that compare to SNP frequency in mouse strains? (The number of SNPs in the VCF is reported in a supplementary table but not discussed in the main text). This point is extremely important: as the authors mention, it is not possible to demultiplex samples from the same mouse strain. Inbreeding is relatively common in laboratory species, even unconventional ones; therefore, information on genetic relatedness and SNP rate would help readers assess whether SNP-based demultiplexing has a good chance to work in their systems. Addressing this point does not require any additional experiments, and computing from the single-cell reads how many SNPs distinguish the individuals pooled here should be straightforward.”

__Our response: __We appreciate the comments raised by reviewer #3.These are valuable critiques and will greatly improve the manuscript.

Planned revisions:

We will expand our Discussion with a paragraph on the limits for genetic differences required for SNP-based demuxing to work, as mentioned in response to Reviewer 2. This will include references to Table 1 values on SNP numbers utilized in each analysis, and hypotheses on the absolute limits for genetic relatedness. We will expand Table 1B to include green monkey. As mentioned in response to Reviewer 2, if previously published data we will also try applying souporcell to data from an inbred mouse line to test run an extreme case of applying SNP-based demuxing to data from very inbred animals. We will more clearly annotate the known relationship between individuals in our experiments, and will discuss this within our Discussion. We will contact the zebrafish and axolotl authors and ask if these animals were siblings. We will identify and apply a method for quantifying the genetic relationship between individuals in each scRNA-seq experiment in this study, to enable us to provide readers with a quantitative measure of genetic diversity present in each experiment. This analysis should shed some light on the requirements for genetic variability in order for SNP-based demultiplexers to succeed.

Reviewer #3:____

“Moreover, the relatively limited number of samples pooled does not validate the use of souporcell with a larger number of samples. For example: in developmental studies, often dozens of embryos are collected and pooled. What are the potential caveats of using souporcell for demultiplexing larger number of samples? The Discussion would be a good place to warn potential users of the limitations of the approach.”

__Our response: __We agree this could still be a limitation, and for developmental studies with multiple dozens of samples, further exploration of optimal demultiplexing methods or the combination of computational and wet-lab based demux methods may be required.

Planned revision:

We will expand our Discussion on predicted limits for SNP-based demuxing of high sample pools, as discussed in response to Reviewer 2. We agree that developmental projects often involve pooling large numbers of samples, so it is worth clearly outlining the benefits and risks of planning to use SNP-based demultiplexing on such high sample pools, and to outline the limits as discussed by the developer of souporcell. As stated above, we will work to identify a previously published pooled zebrafish dataset with multiple dozens of samples and run souporcell on it. While this will not provide any validation it will at the least determine if we are able to assign cell origins, which have thus far been very reliable when assignments have been made.

Reviewer #3: Minor comments:

“- is the accuracy of doublet detection rate a function of number of samples? This can be tested by repeating the monkey in silico experiment with three individuals.”

__Our response: __This is a good question. We do not thing that the number of samples substantially affects the accuracy of doublet detection by souporcell, but we will test this.

Planned revision:

As suggested, we will repeat the monkey analysis with 3 samples to see how this changes doublet detection. Overall, due to the low quality of doublet detection by souporcell found in this manuscript, we will expand our Discussion of doublet detection to propose some potentially useful recommendations for making conservative doublet calls with souporcell external programs (addressed above in response to Reviewer 2. We expect that the more substantial filtering of the monkey datasets relative to the zebrafish dataset prior to pooling contributed to this question. To make these differences more obvious we will more deliberately emphasize the differences in dataset filtering for each experiment.

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

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

From Reviewer 1:

“More generally, showing more direct evidence for the variability of different cell types (not just the immune system) could be informative for scRNA-seq users.”

__Our response: __We do not plan to conduct extensive analyses of other published single cell datasets to provide a further reason for why it is important to have biological replicates for single cell experiments. When building this manuscript, we chose not to pursue the option of publishing an analysis of published single cell datasets in which we could identify artifactual results and animal to animal variability, because we worried that this would be harmful to future open science efforts, and therefore, counterproductive. Further, past papers have already demonstrated the issue of batch effects and animal to animal variability in scRNA-seq datasets, and the requirement for biological replicates to facilitate differential expression analysis. As mentioned above, we will do a better job citing the papers that address these points.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript, Cardiello and colleagues address the problem of demultiplexing pooled samples in single-cell RNA sequencing (scRNAseq) experiments. The manuscript benchmarks the use of a preexisting SNP-based demultiplexing tool, called souporcell, in pooled samples from non-conventional laboratory species. The validation includes computational pooling of published data from different individuals (zebrafish, green monkey), and generation of new pooled data with independent ground-truth information available (with frogs and three salamander species). The authors conclude that souporcell is suitable for demultiplexing scRNAseq data collected as pools from different individuals. The authors propose that SNP-based demultiplexing can be used to monitor and correct for batch effects, whenever data need to be collected as pools (for example: small sample sizes, developmental datasets etc).

Major comments:

The manuscript makes a convincing case for the ability of a preexisting SNP-based demultiplexing tool, called souporcell, to demultiplex pooled samples. The study uses three methods for validation: 1. In silico data pooling; 2. Pooling of transgenic lines; 3. Pooling of cells tagged with CMOs (10x genomics). The results are consistent across experiments.

The authors propose that souporcell is a solution for demultiplexing pooled samples whenever sample tagging methods are not feasible. Although the authors test this approach in several species and conditions, the validation does not cover all possible cases and situations, obviously. Indeed, the authors recommend potential users to run pilot validation experiments with a secondary demultiplexing methods.

However, the manuscript would become more useful if the following points are addressed:

First, what is the genetic relatedness of the individuals pooled in the experiments? What is the SNP frequency in the samples analyzed, and how does that compare to SNP frequency in mouse strains? (The number of SNPs in the VCF is reported in a supplementary table but not discussed in the main text). This point is extremely important: as the authors mention, it is not possible to demultiplex samples from the same mouse strain. Inbreeding is relatively common in laboratory species, even unconventional ones; therefore, information on genetic relatedness and SNP rate would help readers assess whether SNP-based demultiplexing has a good chance to work in their systems. Addressing this point does not require any additional experiments, and computing from the single-cell reads how many SNPs distinguish the individuals pooled here should be straightforward.

Moreover, the relatively limited number of samples pooled does not validate the use of souporcell with a larger number of samples. For example: in developmental studies, often dozens of embryos are collected and pooled. What are the potential caveats of using souporcell for demultiplexing larger number of samples? The Discussion would be a good place to warn potential users of the limitations of the approach.

Minor comments:

• is the accuracy of doublet detection rate a function of number of samples? This can be tested by repeating the monkey in silico experiment with three individuals.

Significance

The manuscript presents a technical advance, by validating the use of souporcell for demultiplexing scRNAseq data collected from non-conventional animal species.

The audience potentially interested in this paper is relatively broad. Potential readers include biologists that collect and analyze scRNAseq data from pooled samples, for instance scientists working in the fields of embryonic development and evolutionary developmental biology, but also clinical researchers. The manuscript will be particularly interesting for scientists working on amphibians, because souporcell is validated experimentally in three amphibian species.

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Referee #2

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). Please place your comments about significance in section 2.

This study provided a SNP-based demuxers to facilitate effective experimental design of scRNA-seq. This model used discrepancies in SNPs across species or individuals to trace back the source of cells in scRNA-seq experiments. Benchmarking the performance of demultiplexing, this study analyzed in silico or experimentally pooled scRNA-seq data from species including zebrafish, African green monkeys, Xenopus laevis, axolotl, Pleurodeles waltl, and Notophthalmus viridescens. It demonstrated that high accurately demultiplex can be achieved regardless of existence of genome and a common SNP set. Overall, this study provided an economical, powerful, and less-biased pooled scRNA-seq data analysis method, depending minimally on the availability of genomic resources.

Major comments:

1. SNP-based demultiplexing performed well on some species, such as zebrafish and Africa green monkey, from which over 90% of the cells analyzed were correctly identified. However, this accuracy decreases in Pleurodeles samples when a common SNPs VCF file is absent (Fig.3). It showed that cell identity can be more precisely defined with the increase of average read depth (Fig 3B). So, I am wondering whether the mis-defined cells shown in Fig. 3E, actually are cells with lower reads. It is better if the authors can test such a correlation between the cell identity and the depth of reads using the data from Fig. 3E.
2. Please discuss limitations of this approach in the manuscript. (1) To which extent, when SNPs are roughly present in the individuals of same species, SNP-based demultiplexing can be applied, e.g., individuals from an inbred strain (c57bl6 mice) would not work.(2) The authors experimentally tested two newt species using SNP-based demultiplexing. When multiple species are experimentally applied, may the cell/nuclei size variation cause problem?
3. What is the upper limit number of samples when using this model. Please make some estimation or discussion about it.

Minor comments:

1. Please add an algorithm principle of this model.
2. Give a clear definition of doublets including the ground truth and Souporcell result.
3. Authors should indicate the time cost of running one round of such analysis, the minimal computational requirements?

Significance

1. Accurate demultiplexing of pooled data can reduce the batch effect between data and experimental costs.
2. This model will achieve good results in analyzing cell evolution between different species, or individuals of same species carrying sufficient SNPs.
3. It is sufficient to run this analysis only with a de novo transcriptome, opened the possibility of using pooled sc-RNA analysis on less-investigated species.

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Referee #1

Evidence, reproducibility and clarity

Cardiello et al tested if souporcell (https://pubmed.ncbi.nlm.nih.gov/32366989/) can be used to demultiplex samples for some model organisms, based on identified SNPs. For this, they used synthetic multiplexed data, publicly available datasets and some new datasets, spanning samples from five model organisms. Their analysis indicates that souporcell could be used to demultiplex scRNA-seq experiments for multiple species, which offers a cost-beneficent approach.

The manuscript reads well and shows this approach can work for different model organisms. However, unfortunately, I am confused about the amount of novelty in this manuscript. The method, souporcell, is already published. The authors indicate souporcell is not validated in non-human samples, but the original paper states that their method works with malaria parasite data (Fig 3b, FigS4). Adapting and using an available tool for different model organisms is good and groups working on different model organisms may find this manuscript useful, but the same could be said for the original article. Due to these reasons, I am not sure whether this manuscript has novelty sufficient for publication. I also wrote down two minor points below:

1. Doublets assigned by souporcell compared to the fluor-based assignment look random. In Fig 2 doublet recovery rate looks smaller, and in fig 3 doublet rate prediction looks more random. This is a bit confusing. Is there any explanation for this?
2. The authors discussed the immune system cells might show some variability in their discussion (referring to fig 3), but this is not clearly shown in the figures as data. Having a percentage bar graph could make it clearer for the readers. More generally, showing more direct evidence for the variability of different cell types (not just the immune system) could be informative for scRNA-seq users.

Significance

scRNA-Seq is becoming a routine approach to assay gene expression profiling. However, it remains costly. There are new approaches to multiplex and demultiplex samples to decrease the cost. Thus, it is good to see that one available tool works for five different model organisms.

Although it is good to see an available tool works for 5 different species, I am not sure about the novelty presented in this manuscript. Technical advances are not clear to this reviewer, as the method is already published. Moreover, this is a technical report manuscript and there is no biological conceptual advance. As a developmental biologist using single-cell mRNA sequencing, someone more directly from the single-cell field may have further comments on novelty, recommendations for references, and could comment on computational aspects in more detail.

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Reply to the reviewers

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

The manuscript "An Sfi1-like centrin interacting centriolar plaque protein affects nuclear microtubule homeostasis" by Wenz and co-authors describes the detection and analysis of the Sfi1-like protein in apicomplexan parasite Plasmodium falciparum. The authors examined the protein localization and function in asexual stages during parasite replication in the red blood cells. The authors detected PfSlp in the PfCentrin1 pulldown, created PfSlp conditional knockdown strain, and evaluated growth and morphological deficiencies associated with the PfSlp deficiency. The study's primary finding is that PfSlp inhibits the extension of nuclear MTs.

Major comments

The key conclusion is appropriate but is poorly supported by experimental evidence. The transitional, experiment-to-experiment conclusions are preliminary and may require additional experiments. The authors did not present a convincing model of the PfSlp1 function in mitosis.

We appreciate the reviewer’s evaluation that our key conclusions are appropriate, but also have taken some of the valid comments below into account and added some conclusive experimental data and partly modified the choice of words when interpreting the data. We are now fully convinced that our conclusions are appropriate and supported by experimental evidence. To understand the function of PfSlp, which was described for the first time in this study, precisely will require a more detailed model of the still very much understudied malaria parasite centrosome and will be the subject of future inquiries.

If PfSlp inhibits the MT polymerization, then the PfSlp reduction should lead to an extension of the bipolar spindle, which is partly supported by longer MTs in the hemispindles. How is the excess of the nuclear MTs prevent the spindle resolution in anaphase?

Intranuclear hemispindle microtubules are indeed elongated. Increased microtubule polymerization does not necessary lead to an increased spindle length but could just as well promote the nucleation of multiple short microtubules or increase overlap between antiparallel microtubules. We, however, want to emphasize that our key conclusion is that PfSlp is implicated in the regulation of nuclear tubulin levels, rather than “inhibits extension of nuclear MT”. In our view this is an important distinction since microtubule misorganization is merely a consequence of changing nuclear tubulin levels. At no point we want to suggest that PfSlp somehow directly inhibits polymerization of microtubules and therefore did not provide any specific evidence. The fact that PfSlp and microtubules are in different compartments underlines this. Yet, we have noted that our abstract uses the word polymerization. Although we mention that it occurs as a consequence of increased tubulin concentration, which thermodynamically favors microtubule polymerization, we acknowledge that this could be misleading and removed this term (line 30). Concerning how the excess nuclear MTs prevent anaphase spindle resolution we propose several explanations in the discussion (lines 381ff). All line numbers refer to document with “tracked changes”.

Fig 4C misrepresents mitotic phases: bipolar spindle should be broken into two in anaphase, while the drawing shows one elongated spindle connecting two poles.

Indeed, we frequently observed, anaphase spindles being “split” ourselves (Simon et al. LSA, 2021, Fig. 2A). Although sometimes we would see one elongated spindle and sometimes more than two as in Liffner et al. 2021 Fig. 3A. For simplicity we only drew one elongated interpolar microtubule bundle but have now corrected this for more accurate representation.

The authors should correct the use of terminology. Throughout the manuscripts, the parasite division stages are called life stages. Life stages are merozoites, gametocytes, ookinetes, sporozoites, etc. The division stages apply to a single life stage and, in the case of schizogony, are rings, trophozoites, and schizonts.

We once falsely referred to life cycle in line 182 when we should have referred to the intraerythrocytic development cycle. The paragraph using the incorrect wording was removed in the revision.

Please, note that schizogony does not follow the ring and trophozoite stages (line 119); it includes them as the distinctive morphological stages of one round of schizogony. The cell cycle terminology is incorrectly applied.

We have the impression that the usage of the term schizogony is rather “fluid” in that it is occasionally also employed to just the describe the phase where DNA replication, nuclear division, and cytokinesis occur (hence schizont stage), but we clearly note the more canonical use as equivalent of the asexual intraerythrocytic development cycle as whole. We modified the terminology accordingly (e.g. by employing “schizont stage”) lines 43, 142, 184, 238, 265.

What is the "mitotic spindle stage," "mitotic spindle nuclei, "or "mitotic spindle duration" (Fig. 4B)?

It has now been conclusively demonstrated that nuclei go through independent nuclear cycles with different morphological stages (Simon et al. 2021 LSA, Klaus et al. 2022 Sci Advances). Hence, we use the term “mitotic spindle stage” to contrast it with the “hemispindle stage”, which can be morphologically distinguished using microtubules as a marker and occurs just prior to S-Phase. Consequently, “mitotic spindle nuclei” are nuclei in the “mitotic spindle stage”. “mitotic spindle duration” designates the time nuclei spend in that stage i.e. from hemispindle collapse until anaphase spindle elongation. We have adjusted and more accurately defined the terminology throughout the text and complemented Fig. 1A for clarity.

Minor comments

The PfSlp knockdown is inefficient: the 55% reduction at the RNA level translates into a minor change at the protein level (Fig.2 and S4). The evaluation of the protein changes should be done by western blot analysis with appropriate controls. The intensity of the IFA signal (used in the study) changes depending on the focal plane, as seen in Fig 1D.

Due to the exceptionally big size of PfSlp of around 407 kDa and the low expression levels western blot analysis was not feasible in our hands. For quantification of the IFA signal we used image projections and background subtraction to integrate the signal of the full z-stack containing the entire cell and our measurement was therefore independent of the focal plane. We have now described this a bit more thoroughly in the methods section (lines 620ff). The change in signal as measured by IFA is still clearly significant and shows a reduction of about 45%, which is coherent with the reduction of 55% found by RNA analysis and ultimately results in a specific phenotype.

Growth defects of the PfSlp KD: It is unclear what causes the reduced parasitemia of the GlcN untreated Slp parasites (Fig. 2C and D).

A likely explanation is that the C-terminal tagging of PfSlp already slightly impairs the function of the protein causing a mild growth phenotype that is not observed in wild type although it is not statistically significant (Fig. 2C). Importantly, the reproduced analysis of parasite growth, shown as multiplication rate in Fig. 2C (and growth curve in Fig. S6) now more clearly demonstrates that when normalizing for GlcN treatment and GFP-glms tagging (“3D7 corr.”) the growth defect is still significant and can therefore be attributed to Slp KD and not to tagging or GlcN treatment addition, which on their own do not cause a significant phenotype.

To conclude that the kinetics of DNA replication is affected, the authors will need to perform the real-time measurements of DNA replication forks.

We thank the reviewer for pointing this out and removed the term “kinetics” (line 182, 269).

The presented data supports that fewer S/M rounds were performed by PfSlp lacking parasites but gives no way to determine whether the S or the M phase was affected.

We thank the reviewer for this valuable comment. Our data so far showed that the very first spindle extension, and therefore M-Phase, is clearly affected (Fig. 4A-B). If the first division fails all subsequent S phases and M phases might be affected at the population level. To test whether S-phase is affected we now acquired time lapse imaging of single cells labeled with the quantitative DNA dye 5-SiR-Hoechst and saw no difference in DNA signal increase for PfSlp KD parasites, while nuclear number was reduced, showing directly that M phase rather than S-Phase is affected (Fig. 4C, lines 280ff).

DNA quantification graph (Fig. 2D) is confusing and does not correlate with the quantification of merozoites (Fig. 2E). Why is the DNA intensity of Slp- parasites lower than the DNA intensity of the Slp+ parasites, even though Slp deficient line produces less progeny? Is it possible that you missed the actual peak of DNA replication? Authors may consider more tight time courses with a few additional time points.

This is a good point. We have repeated this experiment with longer sampling time and shorter intervals. We now plot the fraction of cells with DNA content above 2N (also to exclude double infections and cells that arrest prior to the schizont stage) as a measure to see how many cells are replicating (Fig. 2D, lines 175ff). Although the replication peak was, as observed before, shifted by GlcN treatment we found no significant differences in height. Although the lack of PfSlp tagging and GlcN treatment in the 3D7- control might favor the slightly more productive replication. We complement this analysis by plotting the average DNA fluorescence intensity over time (Fig. S7A) and the area under the curve (see below), as an approximation of “total replication activity” and still found no significant differences (Fig. S7B). The fact that the DNA fluorescence intensity peak does not correlate with the slightly reduced merozoite number observed in Fig. 2E is not very surprising as the fixed time point sampling for DNA quantification can’t differentiate between cells slowing or even halting progression and thereby confounding the averages. This limitation of single timepoint population analysis specifically highlight the importance of our time resolved single cell analysis presented later in Fig. 4, which clarifies the phenotype. Further, merozoite number counting does not give any insight about ploidy of the individual merozoites. Considering the significant nuclear division defect we also show in Fig. 4 it is plausible that some merozoites in the Slp KD could be polyploid, while globally replication is not strongly affected.

Given the main claim, the study lacks the spatial-temporal analysis of tubulin described only in words. The tubulin quantifications by WB (Fig. S6) are not convincing, as well as the resulting conclusion of the cell cycle retardation.

We are not completely sure what the reviewer is indicating by a lack of spatial-temporal analysis of tubulin given that we show time-resolved imaging data of tubulin organization in dividing cells and quantify intranuclear tubulin levels. Those data (particularly Fig. 4A) clearly show a retardation in the mitotic spindle stage. We, however, acknowledge that the data on tubulin quantification via western blot could, as Reviewer 2 also points out, be improved through the addition of biological replicates. We have repeated those experiments twice and can now confirm by statistical analysis that total tubulin, aldolase, and centrin protein levels are not affected by Slp KD at 24, 30, and 36 hpi (Fig. 3E, Fig. S8, lines 232ff). This indicates that the increase in intranuclear tubulin is not a consequence of globally increased tubulin expression.

It is unclear how the authors arrived at the conclusion that the mitotic spindle is deficient in PfSlp KD parasites. Fig. 3C does not show visible differences in GlcN treated and untreated parasites.

PfSlp KD parasites show unusual microtubule protrusions branching of the main microtubule mass, which have never been observed in wild type parasites. This should have been indicated more clearly by adding an arrow in Fig. 3C. We further think our observation that the tubulin content in mitotic spindles is almost three times higher on average than in wild type spindles (Fig. 3D) and that those spindles do not properly extend (Fig. 4A-B) justifies this claim.

How many nuclei are in the cells shown in figure 4 and supplemental movies? It seems as if GlcN treated Slp parasites form one long spindle.

In a previous study (Simon et al. 2021, LSA, Fig. 1B) we have demonstrated that the number of distinct microtubule foci, i.e. mitotic spindles, observed in cells corresponds directly to the number of nuclei. Hence we can assume that prior to successful spindle extension in the PfSlpKD there is one nucleus or two nuclear masses that are in the process of separation. We now added some new time-lapse microscopy data of DNA- and tubulin-stained parasites that confirms that arrested Slp KD parasites fail to properly divide their nuclei (Fig. 4C, Mov. S4-5) and confirms our previously published findings about nuclear number.

A majority of PfSlpKD parasites indeed seem to form one long spindle. However, this “long spindle” appears only after a significant time delay during which wild type parasites already have undergone multiple nuclear divisions and could be a downstream effect of this retardation through e.g. increase of total tubulin levels over time (Fig. 3E).

The conclusion of anaphase block is unsupported: the authors need to demonstrate the accumulation of the metaphase nuclei with a bipolar spindle.

Anaphase describes the phase of chromosome segregation and includes the full extension of the spindle, as discussed above, both of which fails in more than half of the PfSlpKD parasites (Fig. 4A, Mov. S3, S5) and is therefore interpreted as “failure to properly progress through anaphase” for the first time in the discussion (line 381). We currently can’t think about a more direct way to demonstrate this than by time lapse imaging of the very first mitosis in individual parasites. Any analysis of populations at later time point or using fixed cells will be skewed by the phenotype occurring in the very early stages of nuclear division.

Reviewer #1 (Significance (Required)):

The eukaryotic centrosome is a microtubule organizing center that guides the segregation of duplicated chromosomes. Despite being an essential regulator of the parasite division, the apicomplexan centrosome remains poorly understood. Recent studies in Toxoplasma gondii (Suvorova et al., 2015) and Plasmodium species (Simon et al., 2021) demonstrated high diversity of the centrosome organization making the studies of microtubule organizing centers in apicomplexans, particularly challenging. Examining the protein composition is one of the ways to uncover organelle function. The current study would help to understand the evolution of the MTOC and mechanisms of cell division in understudied eukaryotic models.

The focus of my research is the apicomplexan cell cycle. I previously showed the bipartite organization of the Toxoplasma centrosome and identified and characterized several centrosomal constituents, including centrin partner Sfi1. Our most recent study presented evidence of the functional spindle assembly checkpoint in Toxoplasma tachyzoites.

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

Summary:

Plasmodium falciparum parasites undergo several rounds of asynchronous nuclear divisions to produce daughter cells. This process is controlled by the centriolar plaque, a non-canonical centrosome that functions to organize intranuclear spindle microtubules. The organization and composition of this microtubule organizing center is not well understood. Here, Wenz et al. identify a novel centrin-interacting protein, PfSlp, that, following knockdown, leads to fewer daughter cells and aberrant intranuclear microtubule homeostasis and organization.

Wenz et al. identify PfSlp via co-immunoprecipitation of P. falciparum 3D7 strain with an episomally expressed PfCen1-GFP, noting PfSlp as a gene of interest based on the presence of several centrin-binding motifs. The authors go forward to generate a transgenic 3D7 strain, equipping PfSlp with GFP and glmS ribozyme, to localize and evaluate the function of PfSlp in asexual blood stage parasites. PfSlp appears to, using immunofluorescence and STED microscopy, localize to the outer centriolar plaque in schizonts, based on its colocalization with PfCen3. The authors show, utilizing the inducible glmS ribozyme knockdown system, that PfSlp is required for proper parasite growth, noting a defect following addition of GlcN. This defect is noted to cause a delay in the initiation of nuclear division, or schizogony. Analysis of intranuclear microtubule dynamics reveal abnormal microtubule organization, specifically an increase in nuclear microtubule abundance and length following PfSlp knockdown. Together, these findings characterize the role of a novel protein, PfSlp, that contributes to nuclear tubulin homeostasis and organization during schizogony.

Major comments:

The major claims made by Wenz et al. are largely convincing with the data provided.

1. One area that requires additional attention is the following: Wenz et al. claim PfSlp and centrin to be interacting partners based on 1) co-immunoprecipitation (without prior protein crosslinking), 2) the presence of centrin-binding motifs in PfSlp and 3) colocalization of PfSlp and PfCen3. This interaction is not interrogated fully and claims specific to this point need to be clarified and described as preliminary. As it is written, Wenz et al. claim PfSlp is required for centrin recruitment to the centriolar plaque but this is not investigated fully. The data show lower levels of endogenous centrin at the centriolar plaque in PfSlp knockdown parasites but centrin protein levels are similar in wildtype and knockdown PfSlp parasites. As is, the phenotype attributed to PfSlp knockdown could be attributed to PfSlp or aberrant centrin recruitment to the centriolar plaque. Experiments manipulating PfSlp centrin-binding motifs would strengthen these claims and elucidate the role of PfSlp apart from centrin. If not included, less emphasis should be placed here.

We agree with the reviewer that additional evidence to demonstrate the direct interaction between PfSlp and centrin would be adequate. Due to the presence of multiple widely spaced centrin binding motifs in PfSlp, which would require multiple highly challenging rounds of genome editing to be modified, we have opted for reciprocal co-IP using PfSlp-GFP (line 139, Fig. S3, see below). The exceptionally large size of PfSlp of 407 kDa and low expression prevented us from detecting it directly on the western blot, but we found a clear centrin band in the Slp IP that was absent in the control.

We have also further qualified our formulation about centrin recruitment depending on PfSlp (lines 138, 146). Finally, we agree that there are many factors downstream of PfSlp that can contribute to the observed phenotype, which might include centrins and will be subject of future investigations.

The 3.5 mM glucosamine has some toxicity in the parental 3D7. Is it possible to use a lower concentration so the growth of 3D7 is unaffected but the grow of the Slp-GFP GlmS parasites is still reduced?

We acknowledge that the used Glucosamine concentration is on the higher end of the classically used range. The slight toxicity of Glucosamine is dose-dependent and only vanishes at submillimolar concentrations. During initial experiments we have found to generate a robust phenotype with 3.5 mM and decided to carry out all experiments at this concentration. We think that the added effect of PfSlpKD over GlcN treatment alone is sufficiently show as e.g. the merozoite number phenotype (Fig. 2E) and the mitotic delay (Fig. 4B) only occurs in Slp+ parasites.

Fig 3E - the quantification of tubulin levels requires biological replicates to have means and error bars.

We fully agree with reviewer 2 (and reviewer 1 who commented along the same lines) and now generated two more biological replicates that allow us to confirm by statistical analysis that total tubulin, aldolase, and centrin protein levels are not affected by Slp KD at 24, 30, and 36 hpi (Fig. 3E, Fig. S8, lines 235ff).

The use of "centrin" is somewhat imprecise throughout. The authors should specific which centrin (PfCentrin1 or PfCentrin3 or others) they are referring to each time in the text.

Thank you for requesting this clarification. We have used “centrin” on purpose but have failed to properly explain our terminology in the text. For the detection of endogenous centrin we use a polyclonal antibody raised against PfCentrin3 (Simon et al. 2021). Due to the very high sequence identity between PfCentrin1-4 we can’t exclude cross-reactivity of any polyclonal antibody. Throughout the field so far polyclonal antibodies raised against Chlamydomonas centrin and Toxoplasma centrin 1 have been successfully used to label centrin pool at the centriolar plaque. Since we can’t distinguish with certainty which of the centrins (PfCen1-4) is targeted we chose the general description “centrin”. We were however able to show that all four centrins (PfCen1-4) colocalize at the centriolar plaque (Voss et al. biorxiv, /10.1101/2022.07.26.501452) and that Plasmodium centrins interact with each other was demonstrated previously (Roques et al. 2019) while the interaction between PfCen1 and PfCen3 was shown in this study. Therefore, this will not limit our conclusions. We now explain this better in the text (lines 132ff) and adjusted the labeling in Fig. 1E.

The mention of the cell cycle checkpoint is an interesting and appropriate point in the discussion. However, the discussion of it in the last sentence of the introduction is less appropriate. It should be removed from line 92-93.

We are excited by the prospects of this study to finally be able to investigate the presence of checkpoint induced delays using time-lapse microscopy, but absolutely agree with the reviewer and have removed the statement in the introduction.

Minor comments:

1. Line 50 - "are remaining unclear" should "remain unclear"

Has been corrected.

Line 65 - "players" is quite informal. A better word should be selected.

Was replaced with “factors”.

Line 223 - "were" should be "where"

Has been corrected.

The delay in schizogony which is observed following addition of GlcN (Figure S5) may be made more convincing if the experiment is performed hours post invasion rather than hours post treatment. The synchronization of the parasites is in question as it is described in the methods.

We have included this data from our initial exploratory analyses and since it was not central to our argumentation, we choose to add it as supplemental figure. After producing further data, we came to realize that the classical morphological characterization using Giemsa-staining partly mispresents the relevant transition from the pre-mitotic to mitotic stages as the onset of first spindle formation and DNA replication can’t be detected. Previous studies have also indicated that parasites which were drug arrested at the trophozoite to schizont transition were morphologically similar to mid- to late schizonts (Naughton and Bell, 2007). In a context that investigates nuclear division phenotypes we feel that this analysis might rather be misleading and that the provided growth assays, DNA replication quantification, and time lapse movies are significantly more informative. Therefore, we have decided to remove the figure altogether. However, we have moved Fig. S7 to Fig. 4 to show the results of the 3D7+GlcN movie quantification in the context of the Slp+/-GlcN results.

In general, data presentation is clear and readable. The growth defect observed following GlcN treatment (Figure 2C) could be made more clear with data normalization to emphasize that which can be attributed to PfSlp knockdown and not GlcN.

This is a good suggestion and we have reproduced the initial dataset (Fig. 2C, Fig. S6, see below) and normalized the 3D7 multiplication rate, which shows the effect more directly than the growth curves displayed before, for Slp-tagging and GlcN treatment (“3D7 corr.”). We still found Slp +GlcN to be the only condition to have a significant reduction in multiplication rate in the first cycle after treatment (24-72hpi) with respect to 3D7 control as well as the normalized 3D7 value (“3D7 corr”).

Line 276 - Why is nuclear tubulin homeostasis more relevant for closed mitosis? This is difficult to understand. It should be phrased differently or provided with additional explanation.

We thank the reviewer for the comment and agree that this is poorly formulated. We were meaning to express that in e.g. mammalian organisms the nuclear envelope gets disassembled during mitosis and thereby removes the need to regulate import of tubulin into the nucleus for spindle assembly. This is a self-evident statement and has been removed for clarity.

Line 316 - "were" should be "was"

Has been corrected.

The identity, source, and dilution for each antibody must be reported for each use in the methods.

We noticed that we had not fully referenced Table S3, where we listed all used antibodies and dilutions, which we have now done throughout the methods section.

Reviewer #2 (Significance (Required)):

The mechanisms by which intranuclear microtubule dynamics are regulated by Plasmodium falciparum parasites are not well understood. Furthermore, the proteins that are present near the centriolar plaque remain mostly unknown. Understanding the role of the Plasmodium centriolar plaque and its members is critical to describing these dynamics and contributes to our growing understanding of schizogony, an atypical mode of cell division mode with several rounds of nuclear division lacking cytokinesis. Therefore, the identification and initial characterization of PfSlp1 is useful for malaria parasite cell division community.

__

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

The work by Wenz and Simon approaches the function of a novel component of the malaria parasite centriolar plaque, a structure whose complexity has begun to be unraveled only recently__, greatly by the same group. __The authors identify a homolog of Sfi1, a centrin binding protein highly conserved in eukaryotes. Sfi1 homologues usually co-localize with centrioles.

As a tool to characterize its function, the authors uses a conditional knock down strategy, based on GlcN addition, to downregulate PfSfi1-like protein (PfSlp). The authors analyze the impact of pfSlp downregulation on cell division progression, and go on detailly characterizing the progression of mitotic nuclear division. In sum the study finds that expression of Slp1 is required for proper progression of cell division in Plasmodium parasites.

The study is well conducted, and the manuscript clearly written. In general terms I found the data shown to support the author's claims. However, I do have a few points of concern to raise, particularly pertaining overinterpretation of the data, and points that need clarification before the manuscript is fit for publication. In particular the authors should explain more clearly how the data based on fluorescence intensity quantifications was acquired and processed, and how this information is intertwined with the expected kinetics of structures measured, along the cell cycle.

We appreciate the positive feedback and the constructive comments made by the reviewer and now adapted our interpretation of the data or provide additional experimental data to strengthen our argumentation as outlined below. Further we have added some detail to the description of our experimental approaches in the methods section.

I outline below major and minor points that require attention,

Major Points

The manuscript stems off the premise that PfSlp interacts with PfCen1. Despite the fact that Sfi1 is a known interactor of centrin, that the identified protein in Plasmodium has centrin binding motifs, and these proteins co-localize, the support for the direct interaction between the two proteins is based solely on the IP/MS result. No reciprocal IP results are shown.

We thank the reviewer for the suggestion and have now added the reciprocal co-IP, which shows a specific interaction between PfSlp and centrin without need for cross-linking (Fig. S3, see also reply to comment 1 by reviewer 2).

Line 118 specifies that co-localization of Slp-GFP with centrin "corroborates their direct interaction." Co-localization most certainly does not show direct interaction. In addition, Figure 1D shows co-localization with Cen3, not with Cen1, which was the only protein shown to have a physical interaction with Slp via immunoprecipitation. Hence, the claim is unplaced and this section should be reworded for clarity.

The reviewer is correct to point out that co-localization even at STED nanoscale resolution does not demonstrate interaction. We have reworded this statement. Cen3 was the only other specific protein found in the Cen1 immunoprecipitation (Table S1) and the interaction between the four centrins Cen1-4 was shown in an earlier study in P. berghei (Rogues et al. 2019). However, as the Reviewer 2 also indicated, we did not clearly communicate what the targets of our centrin antibody are. We, indeed used an antibody raised against PfCen3. Due to the very high sequence identity between centrins it is, however, unrealistic to exclude cross-reactivity between centrins for a polyclonal antibody (as explained in more detail in our response to Reviewer 2). We have added an explanatory statement in the main text (lines 132ff). Our recent finding that GFP-tagged PfCen1-4 all colocalize at the same position in the centriolar plaque (Voss et al. biorxiv, /10.1101/2022.07.26.501452) and our previously published study of the centriolar plaque (Simon et al. 2021) gives us additional confidence that the antibody specifically labels the compartment of interest.

I was surprised to see how little recovery of PfCen1-GFP the authors obtained from their IP experiments. Whilst I understand that a western blot is not quantitative, I wonder, were the amounts of protein loaded onto each lane normalized for comparative purposes in any way? Please comment on this at least in the figure legend so the reader can gage whether the little PfCen1-GFP recovery was a consequence of the IP experiment, or whether the WB is not representative of the actual IP results but rather show a fraction of the recovered material.

We did not determine the total protein concentration (by e.g. Bradford assay) and therefore did not normalize for protein amounts per lane. Instead, we determined the number of infected red blood cells per ml before Saponin-lysis of the red blood cells and loaded protein lysate equivalent to 1 x 107 cells per lane. We now explain this more clearly in the legend for Fig. S1. During the IP, much of the total protein amount might got lost during the washing steps, which might explain the weak Centrin1-GFP band and the absence of a protein signal in the eluate lane by Ponceau staining (neither a signal for Centrin1-GFP nor unspecific protein signal in the Ponceau). We would conclude that the WB, or at least the lane with the eluate, shows a fraction of the recovered material.

If the WB is indeed representative of the actual PfCen1-GFP recovery rates, I suggest you discuss the possible outcomes of having pulled down so little from the total cell lysate - could it be that the recovered proteins are representative of interactions happening only for a subset of soluble PfCen1 molecules? Can the little protein recovery be explained by Cen1 interactions with insoluble cell components such as the cytoskeleton?

As described above, the eluate lane does likely not represent the actual amount of Cen1-GFP that was pulled down and therefore the WB is not representative of the PfCentrin1-GFP recovery rates. Based on our previous studies we are not aware of any cellular PfCen1 pool beside the cytoplasm and the centriolar plaque. Although they might be below the detection limit. The reviewer raises an interesting hypothesis but we don’t have sufficient data to assume an association with the cytoskeleton and verifying this would require extended further studies.

Were other IP conditions tested? Were the same results obtained?

We carried out three PfCen1-GFP IPs. Once without cross-linking as shown in the study and twice with cross-linking. The two IPs with crosslinking had different amounts of targets identified (24 vs 162). While we did not detect PfSlp in the one with the low number of peptides we detected PfSlp in the second IP. In both IPs we additionally detected PfCen2 and PfCen3.

Do you get the same interactors if the IP is done using anti-Centrin instead of anti-GFP?

We did not test an anti-Centrin antibody for IPs as the protocol from the Brochet group was optimized for the highly specific bead-coupled anti-GFP antibody.

Please define how you identified "specific hits." This is, please describe your criteria for determining "specificity." Was it an all or nothing selection approach? Are Cen1, Cen3 and PfSlp significantly enriched? And if so, how did you define "enriched for" in the context of your experiment?

We thank the reviewer for given us the chance to clarify our candidate selection. We specifically selected the Cen1-GFP IP targets without cross-linking since it produced a short list of hits detected by mass spectrometry. We used an all or nothing approach in that we subtracted from that list any protein that was ever identified in a GFP control IP analysis by the Brochet lab using the same protocol (Balestra et al. 2021). This left only three proteins Cen1, Cen3, and Slp, as our “specific” hits. We have modified the text to explain our selection criteria more explicitly (lines 112ff) while avoid using the term “enrichment” since this is an all or nothing selection.

I'm not at all suggesting here that you repeat this experiment. I understand that the focus of the manuscript is the description of PfSlp, and this stands regardless of the IP results. However, I suggest you include a lengthier discussion of the results shown in SFig1 and Fig1, and the limitations of the approach.

We appreciate the assessment by the reviewer that the focus of the manuscript is otherwise and acknowledge that this is not an extensive analysis of PfCen1 interaction partners. We have, as requested, added a comment addressing this limitation in the discussion (lines 331ff).

Line 123 mentions that Cen3 and Slp1 are recruited together only because they co-localize in most cells showcasing hemi-spindles. Please simply keep "simultaneously" here, as this is the only thing you can conclude from your quantification data. Being recruited "together" implicitly means by "the same mechanism", which is not shown by your data.

We agree that simultaneously is more accurate and we have modified the text (line 146).

Please specify which statistical test was used for determining significance in Figure S4, and what *** refers to in this case. It is hard to judge really how different these data sets are in light of the overlapping error bars. Also, what is quantified here? Integrated density from an immunofluorescence assay? How are the data normalized to be comparable? How many replicates did you quantify? Or are the data shown representative of a single experiment? I could not find these details in the M&M section or the figure legend.

We have revisited all figure legends and consistently defining the p-value and number of replicates (usually N=3) and briefly explain the measurement. Further we have extended the methods section to make our image quantification approach clearer.

Also, on the interpretation of these data; If Slp1 causes a delay in cell cycle progression, and taking into account that the fluorescence intensity of Slp1 varies along the cell cycle, with Slp1 intensity increasing as cell cycle progresses from the ring stages onwards, are these comparable measurements? In other words, are you selecting the same stages whereby the same Slp1 intensities at the centriolar plaque would be expected?

If I understand correctly these measurements are carried out at 55hs post GlcN addition (when the growth phenotype starts evidencing itself?). At this time point, the relative abundance of ring and trophozoite stages (stages at which Slp1 is not expected to be detectable at the CP) is considerable higher than that of the control condition, hence a reduction in Slp1 is expected, and a mechanistic claim about recruitment or stability would be incorrect. Please clarify.

As the reviewer correctly points out it is important to normalize for the stages when quantifying the PfSlp intensities. To achieve this, we only selected schizont stage parasites with a similar distribution of cells containing 3-10 nuclei between the conditions to ensure we are looking at comparable stages. We then quantified the integrated density at each individual centriolar plaque, designated by the presence of a centrin signal. Outside of centriolar plaques no PfSlp signal can be detected. As for ring and trophozoites stages, they do not have a discernable centriolar plaque, or at least not with the markers available in the field, and likely do not express PfSlp based on published transcriptomics data (Plasmodb.org). We have revisited the text to make our quantification strategy clearer (line 170, 621ff).

To understand the relative contribution of Slp1 to the growth delay phenotype, please include 3D7+GlcN control in the quantification of stages shown in Fig. S5. Please check how the data shown in Fig S5 was normalized; the 49 and 73hs bars in the -GlcN condition exceed 100%.

As indicated in our reply to Reviewer 2 we only included this data from our initial exploratory analyses and since it was not central to our argumentation, we chose to add it as supplemental figure. After producing further data, we came to realize that the classical morphological characterization using Giemsa-staining partly mispresents the relevant transition from the pre-mitotic to mitotic stages as the onset of first spindle formation and DNA replication can’t be detected. Previous studies have also indicated that parasites which were drug-arrested at the trophozoite to schizont transition were morphologically similar to mid- to late schizonts (Naughton and Bell, 2007). In a context that investigates nuclear division phenotypes we feel that this analysis might rather be misleading and that the provided growth assays, DNA replication quantification, and time lapse movies are significantly more informative. Therefore, we have decided to remove the figure altogether. However, we have moved Fig. S7 to Fig. 4 to show the results of the 3D7+GlcN movie quantification in the context of the Slp+/-GlcN results.

What is "centrin signal" shown in Figure 2B? Centrin1? Centrin 3? Please clarify which centrin protein you are referring to throughout the manuscript, or provide evidence that they could be interchangeably used for localization and intensity measurement experiments.

We thank the reviewer for pointing out this vagueness. As explained above in the second major point and in the reply to reviewer 2 we use the term “centrin” to emphasize that we cannot be certain to which degree PfCen1,2,3 or 4 contribute to the signal. Our recent preprint (Voß et al. 2022) and Roques et al. 2019 and Simon et al. 2021 however suggest that all centrins co-localize and interact at the outer centriolar plaque. As mentioned we now discuss this in the text (lines 130ff).

Line 149 outlines that Slp1 and centrin intensities are simultaneously reduced, and that this fact alone "affirms" they are part of one complex, and that this implies that Spl1 is somehow involved in centrin recruitment. This claim is not supported by the data shown. There are multiple possible explanations as to how the intensities of both proteins could simultaneously decrease without them conforming the same structure, the same complex or even directly interacting. For example, if the centriolar plaque homeostasis is altered, or the "intensities" are simultaneously dependent on cell cycle progression, they will both be affected without necessarily ever interacting. In fact, if the centrin intensity monitored is that of Cen3, a direct interaction between Slp1 and Cen3 is not demonstrated at any time. At best, the authors could argue that both proteins are directly interacting with Cen1. Again, even this is no definitive proof that they form the same complex.

The reviewer is correct to point out that there are multiple explanations for the decrease of centrin and Slp signal and we have phrased some of the relevant statements more carefully (lines 138, 146, 172). We, however, think that our new reciprocal co-IP data (Fig. S3) in combination with the already provided evidence now significantly strengthens our claim about the interaction between centrin and Slp.

Measurements of DNA content, shown in Figure 2D, show that +GlcN Slp1 knockdown parasites exhibited reduced DNA amounts at 42hs post induction. These results are interpreted as "defects in nuclear division," however, 1. Nuclear division is not analyzed directly, but rather approximated by measuring DNA content. 2. Even in the presence of perfectly normal nuclear division, the DNA content reduction for these parasites at this time point is expected, as cell cycle progression is affected.

Line 160 states that a reduction in merozoite number corroborates a defect in nuclear division. However, the data shown only quantifies merozoites per schizont. As mentioned above, nuclear division is not directly assayed.

We thank the reviewer for emphasizing this important distinction (alongside Reviewer 1). Making the conclusion about nuclear division based on the reduced number of merozoites was premature and we now phrased this more carefully (line 198). Even our data showing inhibition of spindle extension (Fig. 4A-B), although being a strong indicator, do not strictly speaking observe nuclear division. Hence, we have added time-lapse imaging data of nuclear number in KD vs control conditions using the quantitative live cell DNA dye 5-SiR-Hoechst (Fig. 4C. Mov. 4-5). These data now clearly show that the nuclear division or M-phase is affected, while the increase of DNA signal, which represents replication, is not distinguishable from the control. This confirms that nuclear division is the initial and relevant phenotype.

What the nuclear division defects observed are is unclear. Is there fusion, fission? loss of nuclear content? defects in mitosis completion? defects in DNA replication? A reduction in merozoites per schizont, with a concomitant reduction in overall DNA levels could also be explained by a general arrest in the final stages of division. Do other processes linked to nuclear division progress normally? For example, is there daughter cell formation during schizogony without the expected accompanying nuclear division? Are daughters forming in the correct number and position? Are there more daughter cells than nuclei? Or are parasites dying before completing schizogony and producing merozoites? These possibilities need to be carefully teased out before a nuclear division defect can be assigned as the sole causing factor of the division phenotypes observed.

These are all very pertinent questions some of which go beyond the scope of this very first characterization of PfSlp function but we are keen to include those in our future analysis. Some of them we can answer while I will try to offer an interpretation for the remaining ones:

It isn’t fully clear to us what is meant by “Is there fusion, fission”. We will assume that the reviewer refers to the process of karyofission where the nuclear membrane is constricted and fused between the segregating chromatin masses. The field is still lacking a nuclear membrane marker, which makes a direct analysis of this question difficult. Under normal circumstances it has been demonstrated that mitosis is fully closed and the nuclei are completely surrounded by membrane right after division (Klaus et al. 2021). To maybe clarify further we use the term nuclear division to designate the formation of two physically distinct nuclei from one progenitor. We can’t and don’t comment on the integrity of the nuclear membrane and if we had to speculate, it is probably not affected.

Our new data on DNA dynamics (Fig. 4C) shows a delay in nuclear division while DNA replication seems unaffected in the early division stages. The failure to complete mitosis is also shown by the lack of proper spindle extension. It is possible that PfSlp KD affects final stages of division, but since we treat parasites at ring stages and detect a strong phenotype already at the very first division which occurs only a couple of hours after centrin/Slp recruitment one must assume that this is the defining phenotype, which likely has repercussion on later rounds of division. This makes it virtually impossible to clearly define late phenotypes. We actually have to assume that parasites that proceed to later stages of division do so because PfSlp KD was less efficient.

Our data directly shows that more than half of our PfSlp KD parasites “fail to properly divide their nucleus” in the first round of mitosis and therefore can’t construe any other way than to designate this as a “nuclear division phenotype”. We purposefully don’t comment on potential later phenotypes and an impact on cytokinesis (budding) but look forward to investigating this in the future.

Minor Points

• Line 49: consider "...mechanisms remain unclear" instead of "... mechanisms are remaining unclear"

We have corrected this sentence as suggested.

• Readers not familiar with Plasmodium cell division would benefit from having the different stages shown schematically in Figure 1A labeled (ring, merozoite, trophozoite, etc.)

Good suggestion. We have expanded the labeling in Fig. 1A, but still choose to focus on the division stage, which is relevant for the presented data.

• Figure 1 legend: Please specify that "centrin" staining is approximated by centrin 3 specifically. Figure 1E is missing a legend in Figure 1's legend.

Thank you for pointing this out. We have expanded the figure legend accordingly.

• To ease the reader's interpretation of the data, please consider using a different color for 3D7 +GlcN in the plots shown in Figure 2. It is difficult to distinguish the light magenta from the red color at first glance, especially when the lines are partially overlapping.

We explored many different color combinations and consulted with several colleagues and concluded that the chosen color combination is most suitable to convey the logic of the strains (while accounting for green-red blindness).

• Please clarify how long after GlcN addition are phenotypes assessed - ex. Microtubule cumulative length measurements shown in Figure 3.

We mentioned in the previous Fig. 2 that we add GlcN at the ring stage preceding the schizont stage we analyze but failed to specify that we consistently do so for all experiments. We have added more information in the results (line 221) and to the methods section in more detail.

• For Figure 3C please provide a separate image for the Slp channel alone. The overlay of the green centrin signal and the magenta from the tubulin staining render a yellow signal. It is difficult to appreciate the level of Slp knockdown in these cells. Moreover, in the inset, the label "zoom in" is on top of the centrin signal in green, precluding the proper assessment/observation of any yellow signal left over.

Thank you for this remark. We have removed the centrin signal, which is clearly shown in the main panel, from the zoom ins to render the residual PfSlp signal clearly visible.

• When describing Sf1 in T. gondii, please also cite PMID: 36009009 PMCID: PMC9406199 DOI: 10.3390/biom12081115

When submitting our manuscript this study was not yet published, but we are happy to now include it in the introduction (line 92).

The notion of "checkpoint" is mentioned in the introduction and revisited in the discussion. This is a topic under current discussion/evaluation in the field. As mentioned by the authors, demonstration of a checkpoint implies demonstrating reversibility of the putative checkpoint. Though the authors do not make claims about Slp1 or the phenotypes observed activating a specific checkpoint, the manuscript could be further strengthened if the authors showed that the anaphase arrest is reversible upon wash out of GlcN and restored levels of PfSlp expression. I'm including this comment as a "minor points" because it is a only suggestion. I understand that carrying out these experiments is not within the scope of this work. However, if the authors decided to pursue this, it would certainly strengthen the manuscript.

We highly appreciate the suggestion made by the reviewer and already considered ways to inactivate the putative spindle assembly checkpoint or reverse the phenotype. Wash out of GlcN would theoretically be an option although we are unsure that the kinetics of the subsequent protein synthesis would unfold on a short enough time scale. As suggested by Reviewer 2 we try to remain cautious about directly addressing the checkpoint issue, since e.g. PfSlp due to its localization can’t be a direct component of the checkpoint itself. The mention of “checkpoints” has also been removed from the introduction. We are, however, excited that using our time lapse microscopy protocols there now is a framework to investigate this in more depth in the future.

Reviewer #3 (Significance (Required)):

Plasmodium species lack centrioles, and display a divergent mitosis. It is therefore of interest and relevance to understand the peculiarities of the centriolar plaque, as it likely underlies the ability of Plasmodium to upscale its numbers.

Our molecular understanding of the underpinning factors controlling nuclear and cell division in Plasmodium is limited to a few recent publications. The data presented herein is novel and contributes to the body of work with molecular insight and high resolution microscopy coming on for the malaria field.

My expertise is in cell division in Apicomplexan parasites

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

The work by Wenz and Simon approaches the function of a novel component of the malaria parasite centriolar plaque, a structure whose complexity has begun to be unraveled only recently, greatly by the same group. The authors identify a homolog of Sfi1, a centrin binding protein highly conserved in eukaryotes. Sfi1 homologues usually co-localize with centrioles. As a tool to characterize its function, the authors uses a conditional knock down strategy, based on GlcN addition, to downregulate PfSfi1-like protein (PfSlp). The authors analyze the impact of pfSlp downregulation on cell division progression, and go on detailly characterizing the progression of mitotic nuclear division. In sum the study finds that expression of Slp1 is required for proper progression of cell division in Plasmodium parasites.

The study is well conducted, and the manuscript clearly written. In general terms I found the data shown to support the author's claims. However, I do have a few points of concern to raise, particularly pertaining overinterpretation of the data, and points that need clarification before the manuscript is fit for publication. In particular the authors should explain more clearly how the data based on fluorescence intensity quantifications was acquired and processed, and how this information is intertwined with the expected kinetics of structures measured, along the cell cycle.

I outline below major and minor points that require attention,

Major Points

• The manuscript stems off the premise that PfSlp interacts with PfCen1. Despite the fact that Sfi1 is a known interactor of centrin, that the identified protein in Plasmodium has centrin binding motifs, and these proteins co-localize, the support for the direct interaction between the two proteins is based solely on the IP/MS result. No reciprocal IP results are shown. Line 118 specifies that co-localization of Slp-GFP with centrin "corroborates their direct interaction." Co-localization most certainly does not show direct interaction. In addition, Figure 1D shows co-localization with Cen3, not with Cen1, which was the only protein shown to have a physical interaction with Slp via immunoprecipitation. Hence, the claim is unplaced and this section should be reworded for clarity.

• I was surprised to see how little recovery of PfCen1-GFP the authors obtained from their IP experiments. Whilst I understand that a western blot is not quantitative, I wonder, were the amounts of protein loaded onto each lane normalized for comparative purposes in any way? Please comment on this at least in the figure legend so the reader can gage whether the little PfCen1-GFP recovery was a consequence of the IP experiment, or whether the WB is not representative of the actual IP results but rather show a fraction of the recovered material. If the WB is indeed representative of the actual PfCen1-GFP recovery rates, I suggest you discuss the possible outcomes of having pulled down so little from the total cell lysate - could it be that the recovered proteins are representative of interactions happening only for a subset of soluble PfCen1 molecules? Can the little protein recovery be explained by Cen1 interactions with insoluble cell components such as the cytoskeleton? Were other IP conditions tested? Were the same results obtained? Do you get the same interactors if the IP is done using anti-Centrin instead of anti-GFP?

• Please define how you identified "specific hits." This is, please describe your criteria for determining "specificity." Was it an all or nothing selection approach? Are Cen1, Cen3 and PfSlp significantly enriched? And if so, how did you define "enriched for" in the context of your experiment?

• I'm not at all suggesting here that you repeat this experiment. I understand that the focus of the manuscript is the description of PfSlp, and this stands regardless of the IP results. However, I suggest you include a lengthier discussion of the results shown in SFig1 and Fig1, and the limitations of the approach.

• Line 123 mentions that Cen3 and Slp1 are recruited together only because they co-localize in most cells showcasing hemi-spindles. Please simply keep "simultaneously" here, as this is the only thing you can conclude from your quantification data. Being recruited "together" implicitly means by "the same mechanism", which is not shown by your data.

• Please specify which statistical test was used for determining significance in Figure S4, and what *** refers to in this case. It is hard to judge really how different these data sets are in light of the overlapping error bars. Also, what is quantified here? Integrated density from an immunofluorescence assay? How are the data normalized to be comparable? How many replicates did you quantify? Or are the data shown representative of a single experiment? I could not find these details in the M&M section or the figure legend.

• Also, on the interpretation of these data; If Slp1 causes a delay in cell cycle progression, and taking into account that the fluorescence intensity of Slp1 varies along the cell cycle, with Slp1 intensity increasing as cell cycle progresses from the ring stages onwards, are these comparable measurements? In other words, are you selecting the same stages whereby the same Slp1 intensities at the centriolar plaque would be expected? If I understand correctly these measurements are carried out at 55hs post GlcN addition (when the growth phenotype starts evidencing itself?). At this time point, the relative abundance of ring and trophozoite stages (stages at which Slp1 is not expected to be detectable at the CP) is considerable higher than that of the control condition, hence a reduction in Slp1 is expected, and a mechanistic claim about recruitment or stability would be incorrect. Please clarify.

• To understand the relative contribution of Slp1 to the growth delay phenotype, please include 3D7+GlcN control in the quantification of stages shown in Fig. S5. Please check how the data shown in Fig S5 was normalized; the 49 and 73hs bars in the -GlcN condition exceed 100%.

• What is "centrin signal" shown in Figure 2B? Centrin1? Centrin 3? Please clarify which centrin protein you are referring to throughout the manuscript, or provide evidence that they could be interchangeably used for localization and intensity measurement experiments.

• Line 149 outlines that Slp1 and centrin intensities are simultaneously reduced, and that this fact alone "affirms" they are part of one complex, and that this implies that Spl1 is somehow involved in centrin recruitment. This claim is not supported by the data shown. There are multiple possible explanations as to how the intensities of both proteins could simultaneously decrease without them conforming the same structure, the same complex or even directly interacting. For example, if the centriolar plaque homeostasis is altered, or the "intensities" are simultaneously dependent on cell cycle progression, they will both be affected without necessarily ever interacting. In fact, if the centrin intensity monitored is that of Cen3, a direct interaction between Slp1 and Cen3 is not demonstrated at any time. At best, the authors could argue that both proteins are directly interacting with Cen1. Again, even this is no definitive proof that they form the same complex.

• Measurements of DNA content, shown in Figure 2D, show that +GlcN Slp1 knockdown parasites exhibited reduced DNA amounts at 42hs post induction. These results are interpreted as "defects in nuclear division," however, 1. Nuclear division is not analyzed directly, but rather approximated by measuring DNA content. 2. Even in the presence of perfectly normal nuclear division, the DNA content reduction for these parasites at this time point is expected, as cell cycle progression is affected.

• Line 160 states that a reduction in merozoite number corroborates a defect in nuclear division. However, the data shown only quantifies merozoites per schizont. As mentioned above, nuclear division is not directly assayed. What the nuclear division defects observed are is unclear. Is there fusion, fission? loss of nuclear content? defects in mitosis completion? defects in DNA replication? A reduction in merozoites per schizont, with a concomitant reduction in overall DNA levels could also be explained by a general arrest in the final stages of division. Do other processes linked to nuclear division progress normally? For example, is there daughter cell formation during schizogony without the expected accompanying nuclear division? Are daughters forming in the correct number and position? Are there more daughter cells than nuclei? Or are parasites dying before completing schizogony and producing merozoites? These possibilities need to be carefully teased out before a nuclear division defect can be assigned as the sole causing factor of the division phenotypes observed.

Minor Points

• Line 49: consider "...mechanisms remain unclear" instead of "... mechanisms are remaining unclear"

• Readers not familiar with Plasmodium cell division would benefit from having the different stages shown schematically in Figure 1A labeled (ring, merozoite, trophozoite, etc.)

• Figure 1 legend: Please specify that "centrin" staining is approximated by centrin 3 specifically. Figure 1E is missing a legend in Figure 1's legend.

• To ease the reader's interpretation of the data, please consider using a different color for 3D7 +GlcN in the plots shown in Figure 2. It is difficult to distinguish the light magenta from the red color at first glance, especially when the lines are partially overlapping.

• Please clarify how long after GlcN addition are phenotypes assessed - ex. Microtubule cumulative length measurements shown in Figure 3.

• For Figure 3C please provide a separate image for the Slp channel alone. The overlay of the green centrin signal and the magenta from the tubulin staining render a yellow signal. It is difficult to appreciate the level of Slp knockdown in these cells. Moreover, in the inset, the label "zoom in" is on top of the centrin signal in green, precluding the proper assessment/observation of any yellow signal left over.

• When describing Sf1 in T. gondii, please also cite PMID: 36009009 PMCID: PMC9406199 DOI: 10.3390/biom12081115

The notion of "checkpoint" is mentioned in the introduction and revisited in the discussion. This is a topic under current discussion/evaluation in the field. As mentioned by the authors, demonstration of a checkpoint implies demonstrating reversibility of the putative checkpoint. Though the authors do not make claims about Slp1 or the phenotypes observed activating a specific checkpoint, the manuscript could be further strengthened if the authors showed that the anaphase arrest is reversible upon wash out of GlcN and restored levels of PfSlp expression. I'm including this comment as a "minor points" because it is a only suggestion. I understand that carrying out these experiments is not within the scope of this work. However, if the authors decided to pursue this, it would certainly strengthen the manuscript.

Significance

Plasmodium species lack centrioles, and display a divergent mitosis. It is therefore of interest and relevance to understand the peculiarities of the centriolar plaque, as it likely underlies the ability of Plasmodium to upscale its numbers.

Our molecular understanding of the underpinning factors controlling nuclear and cell division in Plasmodium is limited to a few recent publications. The data presented herein is novel and contributes to the body of work with molecular insight and high resolution microscopy coming on for the malaria field.

My expertise is in cell division in Apicomplexan parasites

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Referee #2

Evidence, reproducibility and clarity

Summary:

Plasmodium falciparum parasites undergo several rounds of asynchronous nuclear divisions to produce daughter cells. This process is controlled by the centriolar plaque, a non-canonical centrosome that functions to organize intranuclear spindle microtubules. The organization and composition of this microtubule organizing center is not well understood. Here, Wenz et al. identify a novel centrin-interacting protein, PfSlp, that, following knockdown, leads to fewer daughter cells and aberrant intranuclear microtubule homeostasis and organization.

Wenz et al. identify PfSlp via co-immunoprecipitation of P. falciparum 3D7 strain with an episomally expressed PfCen1-GFP, noting PfSlp as a gene of interest based on the presence of several centrin-binding motifs. The authors go forward to generate a transgenic 3D7 strain, equipping PfSlp with GFP and glmS ribozyme, to localize and evaluate the function of PfSlp in asexual blood stage parasites. PfSlp appears to, using immunofluorescence and STED microscopy, localize to the outer centriolar plaque in schizonts, based on its colocalization with PfCen3. The authors show, utilizing the inducible glmS ribozyme knockdown system, that PfSlp is required for proper parasite growth, noting a defect following addition of GlcN. This defect is noted to cause a delay in the initiation of nuclear division, or schizogony. Analysis of intranuclear microtubule dynamics reveal abnormal microtubule organization, specifically an increase in nuclear microtubule abundance and length following PfSlp knockdown. Together, these findings characterize the role of a novel protein, PfSlp, that contributes to nuclear tubulin homeostasis and organization during schizogony.

Major comments:

The major claims made by Wenz et al. are largely convincing with the data provided.

1. One area that requires additional attention is the following: Wenz et al. claim PfSlp and centrin to be interacting partners based on 1) co-immunoprecipitation (without prior protein crosslinking), 2) the presence of centrin-binding motifs in PfSlp and 3) colocalization of PfSlp and PfCen3. This interaction is not interrogated fully and claims specific to this point need to be clarified and described as preliminary. As it is written, Wenz et al. claim PfSlp is required for centrin recruitment to the centriolar plaque but this is not investigated fully. The data show lower levels of endogenous centrin at the centriolar plaque in PfSlp knockdown parasites but centrin protein levels are similar in wildtype and knockdown PfSlp parasites. As is, the phenotype attributed to PfSlp knockdown could be attributed to PfSlp or aberrant centrin recruitment to the centriolar plaque. Experiments manipulating PfSlp centrin-binding motifs would strengthen these claims and elucidate the role of PfSlp apart from centrin. If not included, less emphasis should be placed here.

2. The 3.5 mM glucosamine has some toxicity in the parental 3D7. Is it possible to use a lower concentration so the growth of 3D7 is unaffected but the grow of the Slp-GFP GlmS parasites is still reduced?

3. Fig 3E - the quantification of tubulin levels requires biological replicates to have means and error bars.

4. The use of "centrin" is somewhat imprecise throughout. The authors should specific which centrin (PfCentrin1 or PfCentrin3 or others) they are referring to each time in the text.

5. The mention of the cell cycle checkpoint is an interesting and appropriate point in the discussion. However, the discussion of it in the last sentence of the introduction is less appropriate. It should be removed from line 92-93.

Minor comments:

1. Line 50 - "are remaining unclear" should "remain unclear"

2. Line 65 - "players" is quite informal. A better word should be selected.

3. Line 223 - "were" should be "where"

4. The delay in schizogony which is observed following addition of GlcN (Figure S5) may be made more convincing if the experiment is performed hours post invasion rather than hours post treatment. The synchronization of the parasites is in question as it is described in the methods.

5. In general, data presentation is clear and readable. The growth defect observed following GlcN treatment (Figure 2C) could be made more clear with data normalization to emphasize that which can be attributed to PfSlp knockdown and not GlcN.

6. Line 276 - Why is nuclear tubulin homeostasis more relevant for closed mitosis? This is difficult to understand. It should be phrased differently or provided with additional explanation.

7. Line 316 - "were" should be "was"

8. The identity, source, and dilution for each antibody must be reported for each use in the methods.

Significance

The mechanisms by which intranuclear microtubule dynamics are regulated by Plasmodium falciparum parasites are not well understood. Furthermore, the proteins that are present near the centriolar plaque remain mostly unknown. Understanding the role of the Plasmodium centriolar plaque and its members is critical to describing these dynamics and contributes to our growing understanding of schizogony, an atypical mode of cell division mode with several rounds of nuclear division lacking cytokinesis. Therefore, the identification and initial characterization of PfSlp1 is useful for malaria parasite cell division community.

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Referee #1

Evidence, reproducibility and clarity

The manuscript "An Sfi1-like centrin interacting centriolar plaque protein affects nuclear microtubule homeostasis" by Wenz and co-authors describes the detection and analysis of the Sfi1-like protein in apicomplexan parasite Plasmodium falciparum. The authors examined the protein localization and function in asexual stages during parasite replication in the red blood cells. The authors detected PfSlp in the PfCentrin1 pulldown, created PfSlp conditional knockdown strain, and evaluated growth and morphological deficiencies associated with the PfSlp deficiency. The study's primary finding is that PfSlp inhibits the extension of nuclear MTs.

Major comments

• The key conclusion is appropriate but is poorly supported by experimental evidence. The transitional, experiment-to-experiment conclusions are preliminary and may require additional experiments. The authors did not present a convincing model of the PfSlp1 function in mitosis. If PfSlp inhibits the MT polymerization, then the PfSlp reduction should lead to an extension of the bipolar spindle, which is partly supported by longer MTs in the hemispindles. How is the excess of the nuclear MTs prevent the spindle resolution in anaphase? Fig 4C misrepresents mitotic phases: bipolar spindle should be broken into two in anaphase, while the drawing shows one elongated spindle connecting two poles.

• The authors should correct the use of terminology. Throughout the manuscripts, the parasite division stages are called life stages. Life stages are merozoites, gametocytes, ookinetes, sporozoites, etc. The division stages apply to a single life stage and, in the case of schizogony, are rings, trophozoites, and schizonts. Please, note that schizogony does not follow the ring and trophozoite stages (line 119); it includes them as the distinctive morphological stages of one round of schizogony. The cell cycle terminology is incorrectly applied. What is the "mitotic spindle stage," "mitotic spindle nuclei, "or "mitotic spindle duration" (Fig. 4B)?

Minor comments

• The PfSlp knockdown is inefficient: the 55% reduction at the RNA level translates into a minor change at the protein level (Fig.2 and S4). The evaluation of the protein changes should be done by western blot analysis with appropriate controls. The intensity of the IFA signal (used in the study) changes depending on the focal plane, as seen in Fig 1D.

• Growth defects of the PfSlp KD: It is unclear what causes the reduced parasitemia of the GlcN untreated Slp parasites (Fig. 2C and D). To conclude that the kinetics of DNA replication is affected, the authors will need to perform the real-time measurements of DNA replication forks. The presented data supports that fewer S/M rounds were performed by PfSlp lacking parasites but gives no way to determine whether the S or the M phase was affected.

• DNA quantification graph (Fig. 2D) is confusing and does not correlate with the quantification of merozoites (Fig. 2E). Why is the DNA intensity of Slp- parasites lower than the DNA intensity of the Slp+ parasites, even though Slp deficient line produces less progeny? Is it possible that you missed the actual peak of DNA replication? Authors may consider more tight time courses with a few additional time points.

• Given the main claim, the study lacks the spatial-temporal analysis of tubulin described only in words. The tubulin quantifications by WB (Fig. S6) are not convincing, as well as the resulting conclusion of the cell cycle retardation.

• It is unclear how the authors arrived at the conclusion that the mitotic spindle is deficient in PfSlp KD parasites. Fig. 3C does not show visible differences in GlcN treated and untreated parasites.

• How many nuclei are in the cells shown in figure 4 and supplemental movies? It seems as if GlcN treated Slp parasites form one long spindle.

• The conclusion of anaphase block is unsupported: the authors need to demonstrate the accumulation of the metaphase nuclei with a bipolar spindle.

Significance

The eukaryotic centrosome is a microtubule organizing center that guides the segregation of duplicated chromosomes. Despite being an essential regulator of the parasite division, the apicomplexan centrosome remains poorly understood. Recent studies in Toxoplasma gondii (Suvorova et al., 2015) and Plasmodium species (Simon et al., 2021) demonstrated high diversity of the centrosome organization making the studies of microtubule organizing centers in apicomplexans, particularly challenging. Examining the protein composition is one of the ways to uncover organelle function. The current study would help to understand the evolution of the MTOC and mechanisms of cell division in understudied eukaryotic models.

The focus of my research is the apicomplexan cell cycle. I previously showed the bipartite organization of the Toxoplasma centrosome and identified and characterized several centrosomal constituents, including centrin partner Sfi1. Our most recent study presented evidence of the functional spindle assembly checkpoint in Toxoplasma tachyzoites.

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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 an interesting study, Leboutet et al. here make excellent use of CRISPR techniques to investigate the role of C-terminal di-glycine sequences important for lipidation in the two Atg8 orthologs LGG-1 and LGG-2 in the autophagy process and in C. elegans development. A main finding from the study is that the LGG-1(G116A) variant, except for visible LGG-1 punctae staining (likely representing autophagosomes), can perform all functions compared to WT LGG-1, suggesting that these can potentially be uncoupled from membrane conjugation, an unexpected concept.

1) To this end, an unaddressed concern in this study is that it has not been ruled out if LGG-1(G116A) perhaps can still trigger an unspecified entity to associate with membranes. Specifically, the authors identify a lower band (referred to as an unexpected, minor band) in Fig 1C for G116A and G116AG117A, but do not investigate the nature of this band (noting, importantly, that these two mutants show normal development). Immuno-EM could be very useful here.

2) Importantly, all of the different LGG-1 mutants are not equally investigated (as done in Fig 1F-K), which is a missed opportunity for the study overall (eg G116AG117* in Fig. 2M and 4). In particular, comparative Western blots are missing for all of the different proteins.

3) Lastly, the study is missing a discussion of the ability of LGG proteins to dimerize (not mentioned at all), a deeper analysis of LGG-2 (later stages than 15 cells, Fig 5D, and of even more significance, EM of double mutants - are there really autophagosomes formed in these?), as well as a more in-depth investigation of ATG-4 interactions (atg-4 investigated only in Fig. 1N, but then never again), which could also help address possible mechanisms involving differentially interacting binding partners.

4) Other discussion points worth further elaboration includes how removal of paternal mitochondria in the absence of autophagosomes without LGG-1 and LGG-2 could take place (again, what does EM look like? This is a particularly important implication of this study, which warrants further study), as well as how the new study's finding possibly impact the use of transgenic C. elegans GFP::LGG-1 markers, including a G116A marker that the authors have published and used as a negative control.

Other relevant points:

1) Fig 2N and S2D are replicated.

2) Error bars are missing in Fig 3I.

3) Fig. 5K should be quantified over multiple repeats.

4) Fig 7 feels like almost 'walking' backwards, may be more efficiently integrated elsewhere in the manuscript (it is also not clear why lgg-2 RNAi is used here, instead of the mutants that are used everywhere else in the study?). Moreover, the authors may want to consider discussing Fig 3/development first (considering the reader has been informed that lgg-1 is an essential gene,- to this point, it is only later made clear that the lethal allele has 8% 'breakthroughs - are these the animals analyzed?) and Fig. 6/EM together with Fig. 1.

5) The yeast section is highlighted in the abstract whereas all data are in supplements; overall it could be better integrated. In particular, sequence alignments and Western blots are missing here.

6) Result section should be revisited for clarity and language, including written in past tense.

Significance

Insights into the role of a C-terminal di-glycine sequences in Atg8 is useful for our understanding of how especially Caenorhabtidis species may engage different precursor vs cleaved Atg8 isoforms for various biological functions. In particular, the interesting and novel concept proposed by the authors in this study is that LGG-1 possesses functions independently of membrane conjugation, which may have potential implications the use of lipidated Atg8 reporters as markers, but also how autophagosomes are formed and function more broadly. However, further evidences is needed to support this 'negative' finding, as commented on above.

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Referee #2

Evidence, reproducibility and clarity

Leboutet et al. use a clever strategy to test the role of LC3 modifications in animal cells. They generate an allelic series of cleavage site mutants of the major LC3 isoform in C. elegans, LGG-1. They convincingly demonstrate that a non-cleavable precursor form of LC3(AA) is unable to localize or function during various forms of macroautophagy, embryonic development, adult survival, or cell death/corpse clearance. A pre-cleaved intermediate form of LC3(A*) is also unable to localize or function during various forms of macroautophagy and has neomorphic characteristics visualized by EM and corpse clearance, but fully functions to promote embryonic development. Surprisingly, mutating the predicted cleavage site of LC3(AG) results in defects in localization, but only a mild delay in autophagic flux. Similarly, LC3(AG) mutants show no defects in viability or embryonic development, which the authors show is partially due to the function of the other LC3 isoform, LGG-2.

Major comments:

What is the new LGG form * in Fig. 1C? Does the Mass Spec data give any hints? The authors imply that this is not lipidated, but show no direct evidence for this statement. There are reports of LC3 conjugation to lipids beside PE, such as PS. Could this represent a switch form LC3-PE to LC3-PS? Or simply cleavage and lipidation at G117? The lack of localization to autophagosomes convincingly demonstrates that this form * does not act like the classic form II, which was thought to be the functional form of LC3, but more information about this isoform would be needed to convincingly make the author's conclusions about lipidation.

The text compares the number of omegasomes vs phagophores vs autophagosomes and refers to Fig. 7E-G, but these graphs do not clearly identify the number of double-positive and single-positive populations, making it impossible to interpret this data. A graph similar to Fig. S5A should replace 7E-G to clearly convey this data.

Fig. 7E vs 7P - Why are there twice as many ATG-18 dots in 7P controls? Is one OP50-fed and the other HT115-fed? Or are the strains different? Why this is different isn't clear from the methods and is missing from the worm strain list.

Fig. S4F - I'm not sure of the utility of the LGG-1 rescue experiments in yeast. WT LGG-1 expression doesn't appear to significantly rescue atg8∆ mutants and it's not clear that there is any significant difference between different LGG-1 isoforms, especially given the broken y-axis. Also showing n=1 and missing statistics. The other yeast experiments are more interpretable and these findings do not significantly add to the paper.

Minor comments:

First half of the first paragraph of the introduction is under-referenced. Please cite relevant review articles. Introduction could also be shortened and more to the point.

Missing statistics in Fig. 1L right. Can't conclude it's increased if not significant.

Fig. 1N is not discussed in the manuscript.

Fig. 3 would be improved by maintaining the color scheme from Fig. 2

Fig. 3H and Fig. 4D are showing similar data in opposite ways (viability vs. lethality). For your reader's sake, please use the same measure for the same assay.

There is no 5-cell stage. C. elegans early embryonic stages are 1, 2, 3, 4, 6, 7, 8, 12, 14, 15.

The relative prevalence of LGG-2-I vs LGG-2-II should be presented in Fig. 5K, similar to the analysis of LGG-1 isoforms in Fig. 1C. It appears that LGG-2 conjugation is being altered in various lgg-1 alleles.

Fig. 6H - EM counts are typically represented as number per section area, not section. The size of cell sections can vary by a large amount.

The authors refer to G116AG117 as gain-of-function, but this is confusing given all the LGG-1 functions lost. A more accurate term could be neomorphic, although the authors haven't performed the genetics to test whether the allele is antimorphic (i.e. G116AG117/null).

Why wasn't the double alanine mutant used in any assays past Fig. 3?

Fig. 7R right model - Phagophore membranes need to be connected at the ends - What are the light green circles representing? - Why does the blue G116A mutant localize to the cargo in the model? The author's said they didn't observe any localization.

Why is Fig. 2N identical to Fig. S3D? There's no need to include the same data twice. Also, both contain an error on the y-axis (15 instead of 5).

Discussion - P. 12 - "Our genetic data indicate that form I of LGG‐1 is sufficient for initiation, elongation and closure of autophagosomes". Indicate is an overstatement. The authors do not perform assays for initiation, elongation or closure.

Discussion - P. 12 - "paternal mitochondria could be degraded by autophagosomes devoid of both LGG‐1 and LGG‐2 " - I couldn't find data in this paper where paternal mitochondria are shown to never have LGG-1 or LGG-2 on them. A single time point analysis isn't sufficient to demonstrate that for molecules that dynamically associate and disassociate with membranes.

Significance

This study shatters our existing models of LC3 function. That LC3 could show any function without localizing to autophagosomes or other structures goes against our current understanding of LC3 function, making this study incredibly important for the autophagy field and the myriad autophagy-relevant clinical fields.

My expertise is C. elegans genetics, embryonic development, membrane trafficking, and non-canonical autophagy.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Laboutet et al., titled: "LGG-1/GABARAP lipidation is dispensable for autophagy and development in C. elegans," describes the potential function of a nonlipidated LGG-1 mutant containing a G116A mutation. Comparison of a G116A missense mutation to the lgg-1 null mutation or a lgg-1(G116A>G117*) suggests that there is some function retained in the G116A missense mutation. The authors claim that no foci form in the lgg-1(G116A) mutants and take this to mean that there is no lipidation. Assays for autophagy function are carried out, such as the degradation of paternal mitochondria in the 1-cell and 15-cell embryo, survival after L1 starvation, normal lifespan, and the presence of apoptotic corpses. In all cases, the lgg-1(G116A) mutant clearly shows function. However, how can we be sure that there is no lipidated form? The authors state that not seeing LGG-1 positive dots in the embryos with an LGG-1 antibody is enough to state that this is not a lipidated form of LGG-1. However, this should be confirmed biochemically. If there were absolutely no lipidated form, the authors also would have to confirm that the function that they see in their assays, for example in survival after starvation, or in degradation of paternal mitochondria is indeed autophagy-dependent. Double mutants with the lgg-1(G116A) and a degradation mutant, like epg-5, should eliminate the activity seen in their assays. Otherwise, this activity may be due to another function of LGG-1 that is not autophagy-dependent.

Major questions:

1.Can we be sure that there is no lipidated form? What if another amino acid can be lipidated to a lower extent? If it is not lipidated, how do the authors propose that this LGG-1 mutant is functioning? In the G116A mutants, and G116AG117* mutant, a new band shows in between the LGG-1 I and LGG-1 II forms, does this band have any activity?

2.In Fig. 1, functional assays for LGG-1 dependent autophagy function in the manuscript are the degradation of paternal mitochondria in the 1-cell and 15-cell embryo, survival after L1 starvation, normal lifespan, and the presence of apoptotic corpses. In Fig. 4, the authors show that most of this activity may be due to redundancy with LGG-2, as the starvation survival of lgg-1(G116A) mutants is mostly abolished by the lgg-2 null mutation. Three assays are done to compare the lgg-1(G116A) single to the lgg-1(G116A); lgg-2 null double, and in 2/3 assays there is still activity conferred by the lgg-1(G116A) mutant observed in the double mutants. What if this activity is not autophagy-dependent?

3.In Figures 1F (100 cell embryo) with lgg-1(G116A) mutant, there are light foci visible, clearly not as bright as in the wild-type, but could these be some less lipidated form of LGG-1 with some remaining function? Again, in figure 4J with the lgg-1(G116A); lgg-2 null (15 cell embryo), very light foci accumulate. What are these?

4.In Figure S4F there is a small difference between the atg8 +empty vector and the atg8 +LGG-1(G116A), however there are no statistics shown.

5.There is evidence that the efficiency of degradation by autophagy in aggrephagy is modulated by the composition of the aggregates (Zhang et al 2017). A model has been proposed where PGL-1, PGL-3 and SEPA-1 are mainly degraded via an EPG-2 mediated pathway, however an EPG-2 independent pathway also exists. Which pathway is being used in the LGG-1(G116A) mutant?

Minor points:

1. The manuscript would benefit from some language editing. In page 2, line 5, it reads: "The general scheme is successive recruitment of a series of protein complexes involved in the dynamic of the process through several steps implicating the phosphorylation of lipids..." Here, it should read "dynamics." The authors use this term often and they should refer to "dynamics".
2. The label "1-cell" are missing in Fig. 1B showing the lgg-1() mutant on the left.

Significance

The manuscript reports a truly novel finding and could be potentially interesting to the autophagy research community. Because the authors make a claim that something is not required, the burden of proof is higher and the authors have to unequivocally show that the LGG-1(G116A) mutant is not lipidated.

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Reply to the reviewers

Reviewer 1.

Major point:

(1) The authors rely upon the redistribution of RNA to measure the inheritance of extant RNAs following cell cycle release. Blocking transcription nicely shows new synthesis is not required for this inheritance. This is also consistent with the idea any newly synthesized RNA would be 'dark,' or not EU labeled, but the transcription inhibitor experiments are critical controls and nicely done. As hinted at the end of their discussion, however, a lack of RNA localizing to G1 chromosomes could be formally attributable to differential RNA stability. Might altered RNA stability of NEAT1, MALAT1, or U2 also contribute to the observed altered localizations upon interphase reentry? The authors could use qPCR or measure RNA half-life to test this possibility. These data would nicely compliment the authors' existing FISH experiments and allow them to specifically argue for differential RNA localization.

We have addressed this point by measuring the stability of MALAT1, U2, and NEAT1 in G2 cells after transcription inhibition using RNA FISH. We find that U2 and MALAT1 exhibit very little RNA degradation after 2.5 hours of transcription inhibition, which is consistent with the reported half-lives for each of these transcripts (10 hours for MALAT1 and >24hrs for U2; PMC3337439). We conclude that differential RNA stability cannot account for differential RNA import observed for these two transcripts. In contrast, NEAT1 transcript is almost undetectable after 1.5 hours of transcription inhibition, which is also consistent with the reported half-life of this transcript (22406755, 3337439). Therefore, RNA degradation during mitosis could contribute to a lack of NEAT1 nuclear import in G1. We have included this new data in a modified Figure 2E (text p5 lines 154-166).

Minor Points:

(1) The authors examine published datasets identifying RNA associated with chromatin and state the reason why these data show little overlap is "primarily attributable to purification methodology." This statement seems speculative, and its basis seems unclear.

We have changed the wording of this section to remove unwarranted speculation (p4-5 lines 116-129).

(2) The SAF-A-AA experiments failed to reveal insight into mechanisms of RNA sorting, although they do suggest the AA construct functions as a gain-of-function due to a) increased RNA reincorporated into chromosomes b) dramatic increase of chromosome targeting of SAF-A. These effects make it difficult to interpret the SAF-A-AA data. Related to this point, the analysis of altered RNA distributions relative to SAF-A is underdeveloped. Because the authors only examined one lncRNA (MALAT1), the conclusion that “forced retention of SAF-A on mitotic chromatin does not lead to an increase in the nuclear inheritance of specific transcripts” seems like an overstatement.

We have reworded this conclusion about the role of SAF-A-AA on mitotic chromatin retention to more accurately reflect our findings (p6 line 197). (3) The authors find the U2 spliceosomal RNA is preferentially inherited. Might they speculate why this would be advantageous?

We have added a sentence to the discussion speculating about the importance of U2 inheritance (p8 line 269-271). (4) Optional: it would be exciting to test the significance of U2 RNA inheritance

We agree with the reviewer that this would be an exciting future direction to test. We envision that testing this idea rigorously would require the development of several new degron cell lines and is outside the scope of this study. (5) For Figure 1, please add statistics to figures and legend; add N=cells examined.

We have added a new supplemental Excel spreadsheet that contains the N of cells measured for each experiment and added statistics to figure legends and figures where tests were significant. (6) For Figure 2, single channel panel of U2 RNA should be added. Figure 2E seems to reproduce the same data shown in Figure 2D (right-most columns) shown with different axes.

We have added a single channel image of U2 to Figure 2 and replaced panel 2E with analysis of MALAT1, NEAT1, and U2 stability after transcription inhibition. (7) Figure 3, it is unclear why the authors selected MALAT1 for analysis, but not NEAT1 (or the single (unlabeled) antisense RNA also enriched in the SAF-A IP (figure 2C).

We examined MALAT1 in greater detail because it is the most abundant lncRNA bound by SAF-A and most robust RNA FISH probe. The unlabeled antisense transcript is hnRNPUas1 and was not detectable in DLD1 cells by RNA FISH. (8) Figure 4B, please add statistics to figure and legend.

For this experiment we prefer not to add statistics to the figure. This experiment was performed on a limited number of cells (21 and 8 respectively) and we do not believe that it is statistically appropriate to treat each cell as an independent N. The data confirms results in our previously published work (Sharp et al 2020) using live cell imaging. (9) Methods: in their description of the published lists of chromatin-bound RNAs, the authors should cite those works and provide a data availability statement with the associated GEO

We have cited these works in the text and methods sections and added GEO accession numbers associated with these studies. (p21 line 442).

Reviewer 2

Major comments:

The authors pose an interesting question -- how does nuclear RNA segregate following mitosis. In many ways, the results presented in this manuscript are rather preliminary. Key controls and validation are missing. Because of this, it is difficult to assess the validity of the main conclusions of the study. More specifically:

1. The main conclusion of the manuscript ("about half of nuclear RNA is inherited by G1 cells following division") is primarily dependent on the experiment described in Fig 1A-B. The authors labeled synchronized cells with EU and quantified nuclear signal after release from synchronization. However, key controls are missing. What is the synchronization efficiency of the RO3306 treatment? How many cells in their acquired fields of cells are in G2 vs in other cell cycle stages? Following their drug release, what percentage of the synchronized cells have undergone telophase? What is the potential error rate in identifying the cell cycle stage using their visual imaging analysis? Without these key controls, it is unclear how to interpret the data presented in Fig 1B.

One reason that nuclear inheritance has not been properly addressed in the literature is the difficulty in obtaining pure populations of cells synchronized in telophase or recently divided cells in early G1. There are no drugs available which can uniquely target these cell stages. In addition, the ability of human cells to all release perfectly synchronously from a drug-induced arrest can vary with cell type. For this reason we used a strategy employing synchronization methods designed to enrich cell populations for telophase or early G1 events, combined with single cell analysis of events with the distinct cytological features of each stage. Cells that have recently divided are extremely distinctive and easily identified using a combination of DAPI morphology to assess nuclear size and condensation state and the presence of Aurora-B/Midbody staining to indicate a recent cytokinesis. Our approach of using single cell analysis coupled with quantitative imaging therefore does not require a high efficiency of synchronization in cell populations. To gain confidence that our observations were reproducible we analyzed a large number of cells, performed multiple experimental replicates, and applied statistical tests to the data.

To clarify these important points we have added text to the descriptions of how these experiments were performed (p3 line 72) and added information about the number of biological replicates to all figure legends and number of cell analyzed in each experiment to Supplementary Table 1.

1. The use of transcriptional inhibitors in Fig 1 is really nice and is important for showing that it's not due to new transcription following mitosis. Well done!

2. One potential mechanism that could explain the observed 25% relocalized nuclear RNA is through passive diffusion. That is, a proportion of molecules that are randomly diffusing during mitosis get trapped inside the newly formed nuclear membrane in early G1. This would be considered noise, and not a specific process that actively relocalizes nuclear RNA back into the nucleus. However, the authors' assay does not have a measure of the noise in their system. One potential experiment that may help quantify this noise is to express GFP in their cells, perform the experiment described in Fig 1A, and quantify the nuclear signal after telophase. This quantification would be the lower bound of the random process. A similar experiment with GFP-NLS could be performed to assess the upper bound of the 'inherited' molecules after mitosis. Without this type of control to quantify noise/random diffusion levels, it is unclear how much of the 25% EU signal that the authors detect is specific to the process they are testing.

We appreciate the point that the reviewer has raised. To address this concern we examined the localization of the abundant mRNA b-actin. We examined the fraction of all b-actin FISH signal that is present in the nucleus in G2 and G1 cells following division. If a significant fraction of RNA is trapped in the reforming nucleus then we would have expected the fraction of b-actin in the G1 nucleus to increase. We observed that less b-actin RNA was present in the G1 nucleus, suggesting that passive entrapment of RNA is unlikely to be a mechanism of RNA inheritance. This is consistent with a lack of inheritance of MALAT1 and NEAT1 lncRNAs following mitosis. We have added these results to a new Supplemental Figure 2 and added text describing the results to the Results section of the manuscript (p4 lines 101-113). Additionally, this result is consistent with recent work showing that mitotic chromosomes condense through histone deacetylation and exclude negatively charged macromolecules (PMID: 35922507) and that chromosome clustering by Ki67 in early G1 phase excludes the cytoplasm from the new nucleus (PMID: 32879492). These references and ideas are now included in the results section of the manuscript.

Related to the comment 1 and 2, EU labeling for 3 hrs in G2 cells would label ALL transcribed RNA, which would include mature mRNAs that will be translated in the cytoplasm. That is, this method is not specific to labeling nuclear RNAs only. How much of their signal is from mRNAs that got trapped inside the newly formed nuclear membrane? One way to test this is to measure the nuclear EU signal at later time points following telophase. Presumably, the nuclear transport mechanism would lead to export of non-nuclear RNAs and only the retained nuclear RNAs would contribute to the signal.

Please see our response to point 3 with regard to entrapment. The laboratory that originally described EU RNA labeling demonstrated a 3 hour EU labeling period results in labeling nuclear RNA, and that longer labeling periods are required to visualize EU labeling of cytoplasmic RNAs after export (18840688). We have also observed in our previously published work that the 3 hour period labels nuclear RNA during interphase (33053167, 32035037). The nuclear EU signal reflects RNAs undergoing transcription, nuclear retained RNAs, and mature mRNAs prior to nuclear export.

To identify nuclear RNAs that could be relocalized following mitosis, the authors analyzed data from "two different studies using different methodologies and a total of three different cell lines". From this analysis, the authors "found very little overlap in the chromatin-bound RNAs identified in these studies (Fig 2A)". This analysis seems fraught with problems. What is the rationale for using these studies? How valid is it to compare results from different methodologies and from different cell lines from the DLD-1 cells used in this study?

We analyzed the data from these two studies because they were the only published studies that identified RNAs that were tightly linked to chromatin. We chose to compare the results from three different human cell lines because we sought to identify nuclear RNAs that were cell type-independent, so that we could analyze the transcripts behavior in DLD1 cells. In support of using these two studies all the RNAs that we analyzed were nuclear in our RNA FISH assays.

A known problem of assessing chromatin-bound RNAs is that the level of contamination from cytoplasmic RNAs is highly variable and highly dependent on the assay. Indeed some of the most common contaminants of nuclear RNA assays are sn-, and sno-RNAs, and these are the main classes of RNA that the authors identified as common among the three data sets. What validation was used to assess whether these are the common noise/contaminants in the data?

Our goal in using the two previously published studies was to identify cell type-independent nuclear RNAs that could be studied in detail using FISH. For validation in our study we performed RNA FISH on MALAT1, NEAT1, and U2. We found that each of these RNAs are highly enriched in the nucleus, consistent with previous publications. Since snRNAs function in splicing and snoRNA primarily function in the modification of tRNA and rRNA in the nucleolus it seems unlikely that these are contaminants of nuclear preparations. Each of the published studies performed their own validations of their purification and sequencing methodology. For the purpose of our work nuclear enrichment of a transcript by RNA FISH satisfied our requirements.

One experimental validation that can be performed is biochemical fractionation of EU labeled cells, which would allow for fractionating nuclear from cytoplasmic RNA. The same problems arise with the analysis shown in Fig 3C when comparing SAF-A RIP-seq with this merged list of chromatin bound RNAs.

In support of the nuclear enrichment of each of the transcripts that we examined RNA-FISH analysis demonstrated significant nuclear enrichment. Additionally, many previous studies have shown that each of these transcripts are enriched in the nucleus (U2: 11489914, 10021385, 7597053; NEAT1: 17270048; MALAT1: 12970751, 17270048). New text describing our use of these studies is present in the results section (p4-5 lines 117-129).

Throughout the manuscript, the authors pose their findings as "RNA inheritance" following mitosis. However, this terminology is misleading. In fact, unless RNAs are lost/kicked out of the cell as they divide, aren't all RNAs inherited following cell division since they are present in the new daughter cells? Instead, what the authors mean is that some nuclear RNAs retain their function following cell division by relocalizing back into the nucleus in the new G1 cells, whereas other nuclear RNAs are unable to relocalize into the nucleus, and then presumably turned over by degradation process. The authors should take better care of their terminology throughout the manuscript.

Thank you for pointing this out to us. As the reviewer stated most nuclear RNAs are removed from chromatin during mitosis. Only a subset are reimported into the nucleus. We have modified our wording to clearly state that we are discussing nuclear RNA inheritance by daughter cell nuclei rather than inheritance into daughter cells in general. These text changes can be found throughout the manuscript.

Minor comments: 1. In all of the figures showing quantification of nuclear EU/FISH signal, the colors (red v blue) are not described (not found in the legend or methods). Presumably they are biological replicates, but this should be clearly stated.

We have modified the plots and figure legends to more clearly explain what is plotted (See text in Figure Legends). 2. Is figure 2E the same data presented in Fig 2D but in different y-axis? If so, state clearly

We have removed the data in the previous version of Figure 2E and replaced it with new data examining stability of MALAT1, NEAT1, and U2 in response to Reviewer 1 (p5 lines 154-166).

Figure 3A. This experiment is using the SAF-A-AID-mCherry system. Therefore the label in Fig 3A should be SAF-A-KD (Knockdown) instead of KO (knockout)

We have corrected this in Figure 3. 4. Typo in Fig 4B y-axis. It should be "Chromatin-localized SAF-A" instead of "Chromain-localized SAF-A"

Thank you for pointing this out, we have corrected it. 5. The methods section indicate the "precise N or replicates in indicated figure legends" but none of the figure legends have the N values listed.

We have listed number of biological replicates in all figure legends and included a new Supplemental Table 1 that contains the number of cells measured for each experiment.

Reviewer 3

The authors investigate an interesting question focussed on whether nuclear RNA from the previous cell cycle is present in the subsequent G1. It turns out that this is more complex than expected with some classes of RNA being inherited whilst others are not. SAF-A or HNRNPU had been implicated in this process but the authors suggest that its role is limited.

Figure 1 In panel A the authors write on image SAF-A-mCh. What does this refer to?

We have added information to the Figure legends indicating that this refers to SAF-A-AID-mCherry knocked-in to the endogenous SAF-A locus (see Figure Legends).

Panel B and other panels can the authors present this data as a boxplot or distribution plot to get a better feel of the data distribution spread.

We have modified all the plots in the manuscript to the Superviolin form to provide a clearer depiction of experimental replicates, mean, and standard deviation.

Presumably labelled RNAs are naturally turned over. Have the authors considered that some loss of signal could be because of this?

We have addressed the stability of specific RNAs using RNA FISH. We find that U2 and MALAT1 show essentially no degradation during the time course of our experiments. This data has now been included in an updated Figure 2. We have also modified our text to address this point more clearly (Figure 2E and p5 lines 154-166).

Panel E, have the authors considered labelling RNA before RO3306 treatment? What effect would this have?

We have performed this experiment in RPE1 cells and the presence of RO3306 did not affect cytological detection of transcript labeling. We have not included this experiment in the manuscript because it is performed in a different cell line than we use for the remainder of these studies.

Shouls TI be added before RO3306 washout?

We added transcription inhibitors after RO washout and entry into mitosis because transcription is naturally suppressed during mitosis. We were concerned that transcriptional inhibition in late G2 could lead to failure to properly enter into M phase.

Also, it is unclear what the arrows are pointing at. In panel F there is a difference between the red and blue experiments. In the methods the authors say that inhibition was for either 1.5 or 2 h. Is this the source of the difference?

We have modified the figure legends to state clearly that different colors indicate biological replicate experiments (See Figure Legends). Figure 2 In panel A there are clear differences between the cell lines. Is it right to compare them? Particularly the GRID-seq vs diMARGI? B, how relevant is it focussing on the "42" overlapping RNAs? In my mind this is not very informative.

Our goal with this analysis was to identify cell type-independent chromatin bound RNAs to analyze in greater detail. Therefore, we analyzed three different cell lines because we planned to analyze transcript behavior in DLD1 cells, which were not included in either study. We have explained this rationale in greater detail in a revised version of the text (p4-5 lines 116-129).

D-E, at a glance it is not clear that E is an expanded view of D. It might be easier if the panels were at same height.

We have removed Panel E and replaced it with a new experiment examining the stability of NEAT1, MALAT1, and U2 after transcription inhibition (p5 lines 154-166). Figure 3 Is it correct to describe IAA treated degron cells as a KO? I also could not see a WB showing how complete SAF-A KD was.

We previously characterized these cell lines in great detail (Sharp et al. JCB 2020). We have now provided quantitative measurement of SAF-A-mCherry fluorescence after different times of auxin addition to provide a quantitative estimate of SAF-A depletion (Supplemental Figure 3C).

2 h treatment seems quite short, is this enough time to obtain sufficient knock down? How heterogenous is SAF-A KD in the cell population?

We examined SAF-A depletion by auxin addition at 2 hours and 24 hours and achieve comparable depletion levels. This data in now included in Supplementary Figure 3C. There is some heterogeneity in the KD as is evident in Figure S3C, but these cells are easily identifiable by the presence of SAF-A-AID-mCherry fluorescence.

Previous studies have shown that SAF-A does not like being tagged. How certain are the authors that these cells behave typically?

We have generated two different cell lines (DLD1 and RPE1) where a C-terminal tag is inserted into the both copies of the endogenous SAF-A gene. SAF-A is one of the common essential genes (https://depmap.org/portal/gene/HNRNPU?tab=overview), however each of our cell lines exhibits no growth defects. We have recently shown that C-terminally tagged SAF-A fully rescues SAF-A knockout phenotypes (Sharp et al. JCB. 2020). Additionally, we have also performed RNA-seq (not published) on RPE1, RPE1 with endogenously tagged SAF-A and RPE-1 depleted of SAF-A and rescued with WT SAF-A-GFP and observed no changes in gene expression or mRNA splicing. Based on these assays we are confident that C-terminally tagged SAF-A expressed at endogenous levels functions normally. Figure 4 I'm struggling with the heading, and wonder if this is not supported by the data. Similarly the final sentence "The highly dynamic exchange of SAF-A:RNA complex" does not really provide an explanation.

We have expanded the text in this section to explain this phenotype in greater detail (p7 lines 216-218).

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Referee #3

Evidence, reproducibility and clarity

The authors investigate an interesting question focussed on whether nuclear RNA from the previous cell cycle is present in the subsequent G1. It turns out that this is more complex than expected with some classes of RNA being inherited whilst others are not. SAF-A or HNRNPU had been implicated in this process but the authors suggest that its role is limited.

Figure 1

In panel A the authors write on image SAF-A-mCh. What does this refer to? Panel B and other panels can the authors present this data as a boxplot or distribution plot to get a better feel of the data distribution spread. Presumably labelled RNAs are naturally turned over. Have the authors considered that some loss of signal could be because of this? Panel E, have the authors considered labelling RNA before RO3306 treatment? What effect would this have? Shouls TI be added before RO3306 washout? Also, it is unclear what the arrows are pointing at. In panel F there is a difference between the red and blue experiments. In the methods the authors say that inhibition was for either 1.5 or 2 h. Is this the source of the difference?

Figure 2

In panel A there are clear differences between the cell lines. Is it right to compare them? Particularly the GRID-seq vs diMARGI? B, how relevant is it focussing on the "42" overlapping RNAs? In my mind this is not very informative. D-E, at a glance it is not clear that E is an expanded view of D. It might be easier if the panels were at same height.

Figure 3

Is it correct to describe IAA treated degron cells as a KO? I also could not see a WB showing how complete SAF-A KD was. 2 h treatment seems quite short, is this enough time to obtain sufficient knock down? How heterogenous is SAF-A KD in the cell population? Previous studies have shown that SAF-A does not like being tagged. How certain are the authors that these cells behave typically?

Figure 4

I'm struggling with the heading, and wonder if this is not supported by the data. Similarly the final sentence "The highly dynamic exchange of SAF-A:RNA complex" does not really provide an explanation.

Significance

This is a clear well undertaken study that has made some interesting observations, which will inform future studies.

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Referee #2

Evidence, reproducibility and clarity

Peer review of manuscript "Differential nuclear import determines lncRNA inheritance following mitosis" by Blower et al.

Section A: Evidence, reproducibility, and clarity

Summary:

In this manuscript, Blower and colleagues examine the fate of nuclear RNAs following cell division. Using cell synchronization methods combined with RNA labeling with EU, the authors show that some of the nuclear RNAs synthesized in the previous cell cycle are relocalized to the nucleus of the new daughter cells in G1. To assess which classes of nuclear RNAs could be 'inherited' after cell division, they used bioinformatic analyses of previous studies, and found a small group of non-coding RNAs in common. To validate a few of these, the authors used RNA FISH to quantify nuclear signals of U2, MALAT1, and NEAT1 in G2 and subsequent G1 stages, and found that only U2 seems to be relocalized to the nucleus following division. The authors then tested whether RNA inheritance could be driven by SAF-A by examining the localization of U2, MALAT1, and NEAT1 in G1 when SAF-A WT or SAF-Amutant (retained in mitosis) is present. But they found that SAF-A plays a minor role in this process. Finally, they found that for U2, nuclear import is required for its relocalization to the nucleus in G1.

Major comments:

The authors pose an interesting question -- how does nuclear RNA segregate following mitosis. In many ways, the results presented in this manuscript are rather preliminary. Key controls and validation are missing. Because of this, it is difficult to assess the validity of the main conclusions of the study. More specifically:

1. The main conclusion of the manuscript ("about half of nuclear RNA is inherited by G1 cells following division") is primarily dependent on the experiment described in Fig 1A-B. The authors labeled synchronized cells with EU and quantified nuclear signal after release from synchronization. However, key controls are missing. What is the synchronization efficiency of the RO3306 treatment? How many cells in their acquired fields of cells are in G2 vs in other cell cycle stages? Following their drug release, what percentage of the synchronized cells have undergone telophase? What is the potential error rate in identifying the cell cycle stage using their visual imaging analysis? Without these key controls, it is unclear how to interpret the data presented in Fig 1B.
2. The use of transcriptional inhibitors in Fig 1 is really nice and is important for showing that it's not due to new transcription following mitosis. Well done!
3. One potential mechanism that could explain the observed 25% relocalized nuclear RNA is through passive diffusion. That is, a proportion of molecules that are randomly diffusing during mitosis get trapped inside the newly formed nuclear membrane in early G1. This would be considered noise, and not a specific process that actively relocalizes nuclear RNA back into the nucleus. However, the authors' assay does not have a measure of the noise in their system. One potential experiment that may help quantify this noise is to express GFP in their cells, perform the experiment described in Fig 1A, and quantify the nuclear signal after telophase. This quantification would be the lower bound of the random process. A similar experiment with GFP-NLS could be performed to assess the upper bound of the 'inherited' molecules after mitosis. Without this type of control to quantify noise/random diffusion levels, it is unclear how much of the 25% EU signal that the authors detect is specific to the process they are testing.
4. Related to the comment 1 and 2, EU labeling for 3 hrs in G2 cells would label ALL transcribed RNA, which would include mature mRNAs that will be translated in the cytoplasm. That is, this method is not specific to labeling nuclear RNAs only. How much of their signal is from mRNAs that got trapped inside the newly formed nuclear membrane? One way to test this is to measure the nuclear EU signal at later time points following telophase. Presumably, the nuclear transport mechanism would lead to export of non-nuclear RNAs and only the retained nuclear RNAs would contribute to the signal.
5. To identify nuclear RNAs that could be relocalized following mitosis, the authors analyzed data from "two different studies using different methodologies and a total of three different cell lines". From this analysis, the authors "found very little overlap in the chromatin-bound RNAs identified in these studies (Fig 2A)". This analysis seems fraught with problems. What is the rationale for using these studies? How valid is it to compare results from different methodologies and from different cell lines from the DLD-1 cells used in this study? A known problem of assessing chromatin-bound RNAs is that the level of contamination from cytoplasmic RNAs is highly variable and highly dependent on the assay. Indeed some of the most common contaminants of nuclear RNA assays are sn-, and sno-RNAs, and these are the main classes of RNA that the authors identified as common among the three data sets. What validation was used to assess whether these are the common noise/contaminants in the data? One experimental validation that can be performed is biochemical fractionation of EU labeled cells, which would allow for fractionating nuclear from cytoplasmic RNA. The same problems arise with the analysis shown in Fig 3C when comparing SAF-A RIP-seq with this merged list of chromatin bound RNAs.
6. Throughout the manuscript, the authors pose their findings as "RNA inheritance" following mitosis. However, this terminology is misleading. In fact, unless RNAs are lost/kicked out of the cell as they divide, aren't all RNAs inherited following cell division since they are present in the new daughter cells? Instead, what the authors mean is that some nuclear RNAs retain their function following cell division by relocalizing back into the nucleus in the new G1 cells, whereas other nuclear RNAs are unable to relocalize into the nucleus, and then presumably turned over by degradation process. The authors should take better care of their terminology throughout the manuscript.

Minor comments:

1. In all of the figures showing quantification of nuclear EU/FISH signal, the colors (red v blue) are not described (not found in the legend or methods). Presumably they are biological replicates, but this should be clearly stated.
2. Is figure 2E the same data presented in Fig 2D but in different y-axis? If so, state clearly
3. Figure 3A. This experiment is using the SAF-A-AID-mCherry system. Therefore the label in Fig 3A should be SAF-A-KD (Knockdown) instead of KO (knockout)
4. Typo in Fig 4B y-axis. It should be "Chromatin-localized SAF-A" instead of "Chromain-localized SAF-A"
5. The methods section indicate the "precise N or replicates in indicated figure legends" but none of the figure legends have the N values listed.

Significance

General assessment:

The authors pose an interesting question -- how does nuclear RNA segregate following mitosis. However, the results presented in this manuscript are rather preliminary. Key controls and validation are missing. Because of this, it is difficult to assess the validity of the main conclusions of the study.

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Referee #1

Evidence, reproducibility and clarity

This study follows up on the authors' recent work showing entry into mitosis is associated with RNA removal from condensing chromosomes and investigates whether the same RNAs that were removed are reincorporated into G1 chromosomes. The study is timely and simple yet elegant. The authors use pulse chase experiments to follow the distribution of bulk RNAs in synchronized then released cells, showing a subset of labeled RNAs are reincorporated into chromatin. This process is selective, as the authors demonstrate some RNAs are more likely to reassociate with G1 chromosomes than others. The authors go on to use various small molecule inhibitors to provide mechanistic insights showing transcription is not required for RNA inheritance, but nuclear pore components (importin-B) are.

The study is well conceived and executed. I recommend the following relatively minor revisions.

Major point:

1. The authors rely upon the redistribution of RNA to measure the inheritance of extant RNAs following cell cycle release. Blocking transcription nicely shows new synthesis is not required for this inheritance. This is also consistent with the idea any newly synthesized RNA would be 'dark,' or not EU labeled, but the transcription inhibitor experiments are critical controls and nicely done. As hinted at the end of their discussion, however, a lack of RNA localizing to G1 chromosomes could be formally attributable to differential RNA stability. Might altered RNA stability of NEAT1, MALAT1, or U2 also contribute to the observed altered localizations upon interphase reentry? The authors could use qPCR or measure RNA half-life to test this possibility. These data would nicely compliment the authors' existing FISH experiments and allow them to specifically argue for differential RNA localization.

Minor Points:

1. The authors examine published datasets identifying RNA associated with chromatin and state the reason why these data show little overlap is "primarily attributable to purification methodology." This statement seems speculative, and its basis seems unclear.
2. The SAF-A-AA experiments failed to reveal insight into mechanisms of RNA sorting, although they do suggest the AA construct functions as a gain-of-function due to a) increased RNA reincorporated into chromosomes b) dramatic increase of chromosome targeting of SAF-A. These effects make it difficult to interpret the SAF-A-AA data. Related to this point, the analysis of altered RNA distributions relative to SAF-A is underdeveloped. Because the authors only examined one lncRNA (MALAT1), the conclusion that "forced retention of SAF-A on mitotic chromatin does not lead to an increase in the nuclear inheritance of specific transcripts" seems like an overstatement.
3. The authors find the U2 spliceosomal RNA is preferentially inherited. Might they speculate why this would be advantageous?
4. Optional: it would be exciting to test the significance of U2 RNA inheritance
5. For Figure 1, please add statistics to figures and legend; add N=cells examined.
6. For Figure 2, single channel panel of U2 RNA should be added. Figure 2E seems to reproduce the same data shown in Figure 2D (right-most columns) shown with different axes.
7. Figure 3, it is unclear why the authors selected MALAT1 for analysis, but not NEAT1 (or the single (unlabeled) antisense RNA also enriched in the SAF-A IP (figure 2C).
8. Figure 4B, please add statistics to figure and legend.
9. Methods: in their description of the published lists of chromatin-bound RNAs, the authors should cite those works and provide a data availability statement with the associated GEO

Significance

General assessment: (strengths) The study is timely and simple yet elegant. It is well conceived and executed. In general, the conclusions are supported by the data. The study provides insight into a fundamental basic science process likely of interest to a broad readership. (weaknesses) The authors do provide some mechanistic insight into how RNAs are inherited, although this mechanism will need to be further developed in future studies. The role of SAF-A is unclear. Because those experiments did not produce a clear effect, they seem distracting. The idea that specific RNAs are sorted is exciting, but as yet we do not know how this sorting happens. Future work examining the importance of RNA inheritance should be prioritized. Measuring RNA abundance of the different analyzed RNAs (NEAT1, MALAT1, vs U2) should be added to the current manuscript.

Advance: This study follows up on the authors' recent work showing entry into mitosis is associated with RNA removal from condensing chromosomes and investigates whether the same RNAs that were removed are reincorporated into G1 chromosomes.

Audience: The study provides insight into a fundamental basic science process likely of interest to a broad readership.

Describe your expertise: basic cell biology, RNA localization

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

The manuscript presented the Cryo-EM structure of HECT E3 UBR5. Using Alphafold2 model of UBR5, the authors were able to dock and refine the structure model of full length UBR5. Interestingly, UBR5 exists as a homodimer and could potentially assemble into a larger oligomer based on SEC and Cryo-EM data. The antiparallel arrangement of the homodimer suggests that the C-terminal HECT domain could transfer ubiquitin in trans or in cis configuration. The tetrameric model reveals a ring-like structure with a large central cavity, presumably to accommodate large proteins/complexes. Using AKIRIN2 as a substrate, the authors demonstrated that UBR5 did not ubiquitinate AKIRIN2, but prefers ubiquitin modified AKIRIN2 as the substrate for ubiquitin chain elongation. Indeed, they observed that UBR5 preferentially ubiquitinates pre-ubiquitinated non-cognate substrate and free ubiquitin hinting that UBR5 is a chain elongating E3. Lastly they showed that UBR5 HECT contains a plug-loop that blocks C-lobe rotation and suggested that conformational change is necessary for ubiquitin transfer.

Comments:

1. Homodimerization and oligomerization are the novel aspect of this study but the manuscript lacks validation of the structure. The authors should provide biochemical/mutagenesis analysis to support the dimerization interface observed in the structure. Also the model showed that SBB2 is involved in the tetramerization interface, could the authors verify this by designing a SBB2 deletion mutant?
2. Would be useful to show the docking of Alphafold2 model onto the Cryo-EM map prior to further model building and refinement in the supplementary data.
3. Please show the SDS-PAGE of purified UBR5 used for Cryo-EM study.
4. Figure referencing is not in order. For example Figure 1J was described before Figure 1I. Figure 2A,B mentioned after Figure 2C. Also some Figures are not properly referenced in the main text, e.g. p10 when describing ubiquitin chain formation of UbAKIRIN2 and UbSecurin. Please check throughout the manuscript.
5. Figure legends are missing for Figure 1H-1J
6. It was stated in p10 that there was no binding between UBR5 and UbSecurin in Figure S3C, but Figure S3C showed faint FAM-UbSecurin across the fractions. It would be useful to repeat this with FAM-UbSecurin alone to ensure the faint bands are background signal.
7. In p10, it was stated that UBR5 and UbAKIRIN2 interaction was enhanced in the presence of ubiquitin. How did the authors come to this observation? The sucrose gradients (Figure 3B) showed that UBR5 co-elutes with both AK2 and UbAK2. This reviewer is unclear whether the intensity of the bands can be used to evaluate the strength of the binding affinity. Was the experiment performed at the same protein component concentration/condition? The UBR5 appears to elute at different fractions from the two experiments.
8. The authors suggested that the UBA domain might bind ubiquitin and promote ubiquitination of UbAKIRIN2. It is noteworthy that prior studies on several HECT E3s showed that HECT domain alone can catalyze free ubiquitin chain assembly. Could it be possible that the HECT domain of UBR5 alone could catalyze the extension of UbAKIRIN2, UbSecurin or UbdeltaGG?
9. In Figures 3A and S3B, does the ubiquitin chain elongation occur only on the fused ubiquitin?
10. Figure 4E mentioned in the main text but is missing.
11. It is not clear from Figure 4 whether the plug-loop is blocking the rotation of C-lobe. The overlaid Figure 4 is quite busy, would be useful to show the UBR5 HECT domain alone with other HECT domain presented in the same orientation but in separate panels. With the plug-loop in the current configuration, does it block E2 binding and transthiolation reaction? Figure 5B seemingly suggested that plug-loop is blocking transthiolation but it is hard to visualize. The authors could enlarge Figure 5B and color the plug-loop differently.

Significance

The manuscript provides the structural insight into the organization of UBR5. While the Cryo-EM data largely agrees with the Alphafold2 UBR5 model, this should not take away the significant effort in obtaining the large UBR5 protein structure. The structure reveals an unexpected homodimerization of UBR5 and in the assembly of larger oligomer. The biochemical analyses suggest that UBR5 is proficient in ubiquitin chain elongation. Overall the study provides a structural framework for understanding how UBR5 could function as an ubiquitin ligase. The findings will be of interest to scientist in the ubiquitin field and in understanding UBR5 biology.

Limitation: aside from the structure, the study lacks detailed mechanisms of how UBR5 catalyzes ubiquitin transfer. While few models for ubiquitin transfer were proposed, the study lacks suitable substrates to investigate the mechanism. The study showed that UBR5 can elongate ubiquitin chain, but it is not clear whether UBR5 could transfer ubiquitin to substrate.

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Referee #2

Evidence, reproducibility and clarity

This manuscript reported the CryoEM ring-like structure of the full-length human E3 assembly ligase UBR5, showing its assembly into a tetramer. The authors identified critical determinants for antiparallel homodimer and tetrameric assembly. They further described AKIRIN2 as UBR5 substrate and provided evidences of a preferential interaction and activity of UBR5 towards monoubiquitinated proteins. Based on these findings, they proposed UBR5 as chain-elongating E3 ligase.

CryoEM data are solid, and the model interpretation of the tetrameric structure provides a precise description of the domain composition of the protein that well fit with biochemical data. Additional experiments are suggested to corroborate few statements of the authors.<br /> We believe they are realistic in terms of time and resource.

1. Authors should address the importance of tetramerization by mutating SBB2 at the tetramerization interface and comparing the mutant with wild type in mass photometry and ubiquitination assays. In silico analysis of the interaction interfaces (e.g by using PISA software) could be useful to select amino acids to be mutated. The authors suggested a role for oligomerization in catalysis and mutants are needed in order to define the real "functional unit" of the enzyme.
2. The authors used sucrose gradient sedimentation assay to prove UBR5 and substrate interaction (Fig. 3). Control experiment that showed UBR5 protein sedimentation in presence of GFP only is instead in Supplementary Fig. 3D. Unfortunately, in that panel the signal of UBR5 is not visible. Main figure should be revised showing proper controls of the experiment.
3. The authors need to better clarify the features of the AKIRIN-UBR5 interaction. According to the data, the enzyme is equally active on both AKIRIN-Ub and Securin-Ub, suggesting a Ub-specific engagement. What would be a correct explanation of these results? Is the UBA domain directly involved in this process? Testing the activity of a UBA-impaired mutant should help to solve this issue.
4. The authors identified a 25 aa sequence, called Plug loop, preceding the HECT domain. In the structure it is inserted between N and C-lobe subdomains of the HECT and appears to lock the enzyme in an open L-conformation. These structural findings are interesting, but no supported by experimental data. Which is the effect of the Plug loop deletion in a ubiquitination assay? Without further validation the last chapter of the results remains purely speculative and may better fit in the discussion.
5. The datasets are clearly affected by preferential orientation as showed by the angular distribution and 2D classes (reason why the authors correctly performed data collection with tilt). A comment on this is required in the experimental section. In addition, it is not clear whether the presented maps (Fig 1 and 2) derive from merging of the two datasets or only the model has been built using the two different datasets.
6. As a general comment, authors should enlarge panels in which structural details are described, highlighting the side chain residues involved in binding interfaces. Fig. 5 and Fig. 6 are particularly small and incomplete. Most of the structural figures miss key labels needed for a proper understanding. E.g. among the others, numbering of the helix composing the armadillo domain.
7. The overall organization of the figures is quite confusing. Pag. 7 Figure 2C should represent a "box stabilized by three zinc ions mediated by two histidine and seven cysteine residues" according to text citation, but none of these details is highlighted in the corresponding figure. The eye in Figure 1,2,4 does not mean much if a proper box is not linked to the actual site to be seen. In addition, arrows indicating the rotation axis is hard to interpret. Few panels miss the legend. Figure 1A and many other panels miss the reference in the text. More details below.

Additional points:

• Mass Photometry data need additional comments and labels. Please comment on the MP concentration used to analyze the samples. Being a dynamic system, you are probably seeing an equilibrium of species at 10 nM in MP. For better completeness of MP figures, labels that includes counts, % of species and sigma should be added to the nice representation of oligomers. Which condition/fraction represent the MP data showed in 1B?
• If Alphafold models are mentioned and used for model building, it would be nice to provide at least a pLDDTscore and ptm score. Since some details of the AF model are described in the text, an additional superposition of the AF model with the final model derived by EM would be useful to the community.
• A simple workflow describing the cryoEM data processing that includes how many particles have been used in each step is required, at least in the methods section. The authors need to show the cryoEM 2D classes of the dimer as well.
• Please add the domain boundaries in Figure 1A and highlight the domains on the alignment included in Supplemental Table 1.
• Pag. 8 please decide which abbreviation to use, either UBR or Ubr.
• Page 8, line 192. I found annoying to find the same sentence used by competitors who posted a bioRxiv paper 3 days before the one we are reviewing (doi.org/10.1101/2022.10.31.514604 page 4, line 135).
• In supp. 1C legend, "high concentration of NaCl" is a bit vague
• Complementary to Supp Fig 2A, a zoom in of the density map with traced model would be beneficial to show the actual map quality obtained.
• Pag. 6 lines 133-134, the helix residues involved in homodimerization are cited in the text, but not highlighted in the Figure 1.
• Figure 1 legend, panels H-I-J description are missing.
• Figure 3, panel B, meaning of the asterisk is not reported in the figure legend.
• Figure 4, 5 panels from A to E are cited in the text while figure reported only 4.

Referees cross-commenting

I think all the reviews are fairly consistent and agree with the comments raised by my colleagues with the one exception of Point 3 of Reviewer 1. The issue is certainly important yet the experiment suggested is not clear. I personally have troubles designing an informative experimental set-up.

Significance

This paper presents the intriguing Cryo-EM structure of the full-length HECT E3 ligase UBR5. As it stands, this work provides evidence of the existence of a tetrameric RING-like conformation that could represent the functional unit of the catalysis. Very little validation of the features identified in the Cryo-EM structure is given, thus the paper remains quite descriptive, but in any case interesting and informative for the ubiquitin field.

Considering that UBR5 is a quite competitive subject in these days (e.g. at least one additional Cryo-EM structure was posted in BioRxiv, doi.org/10.1101/2022.10.31.514604), I would positively consider this manuscript for publication if the authors reply in full to the issues raised.

My field of expertise: Ubiquitin regulation and interactions, biochemistry, biophysics and Cryo-EM.

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Referee #1

Evidence, reproducibility and clarity

This manuscript describes cryo EM structural analyses of human E3 ligase Ubr5 in dimeric and tetrameric states. Ubr5 belongs to structurally poorly characterized family of Hect E3 ligases and has important biological functions, e.g. in targeting transcription factors for proteasomal degradation. The manuscript therefore addresses an important subject of basic science and biomedical interest. Using in vitro ubiquitylation assays the authors show that purified Ubr5 forms ubiquitin chains on a substrate (akirin2), but also on a non-substrate (securin), provided the proteins are covalently fused to ubiquitin. The authors interpret this as a preference of Ubr5 for ubiquitin chain elongation over initiation. Consistently they show that Ubr5 forms free ubiquitin chains linked by Lys48 in vitro. Whilst the structures of full-length Ubr5 are very interesting and important, this manuscript appears to be at a premature stage. The structural interpretation and models lack experimental validation and remain speculative. The presented activity assays are interesting but do not quite link up with the structural part which leaves the manuscript somewhat disconnected. In my view this manuscript requires considerably more work to correlate structure with function, as suggested below, but holds the potential of turning into a highly insightful story.

Conceptual comments:

1. Key observation is that a Ubr5 dimer assembles into higher-order oligomers. The authors speculate that this is functionally relevant, e.g. by the possibility of substrate ubiquitylation occurring within the central cavity of the ring shaped tetramer or ubiquitylation in cis and trans. However, neither significance of Ubr5 oligomerisation nor dynamics/determinants in solution is investigated.
   • In line 100, the authors state that individual oligomeric species could not be separated but do not show data. Why can the species not be separated? Do they exchange? Can exchange be controlled by ionic strength/pH/temperature...?<br /> The authors also suggest that the tetramer is transient (e.g. line 165). What is the evidence for this? Subunit exchange may be tested by mixing different species, e.g, containing labels/tags etc.
   • The authors should design structure-based mutations, particularly within the small, tetrameric interface, and measure oligomerisation state of the mutants to correlate their cryo EM analyses with oligomeric states observed in solution.
   • The authors should also subject individual oligomers (if required, by mutational stabilization of particular states) in activity assays to test their hypotheses.
2. Lines 160-163: "We performed extended 3D classification of the tetramer, which allowed us to confidently dock two models of UBR5 dimers. This revealed that the tetrameric assembly of UBR5 is formed by SBB2 domains of two opposite dimers (Figure 1I)." The idea that the SBB2 domains make up tetrameric interface should be experimentally validated.
3. Lines 311 onward: The authors speculate that oligomeric arrangements of Ubr5 allow for substrate modification in trans and cis, expanding the substrate repertoire. As part of results section, this should be experimentally addressed. Depending on the exchange behaviour of subunits within oligomers, it may be possible to use mixing experiments. Alternatively, they authors may consider comparing Ubr5 ubiquitylation efficiency towards substrates of different sizes, which may allow for better interpretation of the distance restraints they defined.
4. Figure 1J suggests that MLLE domain was modelled, yet the authors note in the text (line 190) that this domain is disordered.
5. The interpretation of the in vitro experiments comparing ubiquitylation of ubiquitin fused akirin2 (substrate) and ubiquitin fused securin (non-substrate) require a re-evaluation: The fact that even ubiquitin fused securin is efficiently ubiquitylated by Ubr5 in vitro shows that a fused ubiquitin molecule is sufficient to recruit a protein for modification by Ubr5 (likely via the UBA domain) in vitro. The specificity of Ubr5 for certain substrates in the cell must therefore follow different (unknown) mechanisms. It is possible that observed, additional affinity between Ubr5 and akirin2 (which is independent of ubiquitin) contributes to this. The available data, however, are insufficient to suggest a hierarchy of interactions (suggested in line 235-237). The interpretation should also be adapted in Figure 6 in which an order of binding events is postulated.
6. Fluorescently labelled deltaGG-ubiquitin is used to monitor free chain formation by Ubr5. Why is this setup used rather than a simple assay with full-length ubiquitin? The rationale/benefit should be clarified.
7. Conformation/functional significance of the plug loop should be validated by mutagenesis.
8. The mass spec data should be presented in a compact supplementary figure or table, in addition to comprehensive data table in Suppl. Table 2.
9. Statements without data backup should be phrased as hypotheses or experimentally validated, e.g.,
   • line 27:"Using cryo-EM processing tools, we observe the dynamic nature of the domain movements of UBR5, which allows the catalytic HECT domain to reach engaged substrates."
   • line 31:"This preference for ubiquitinated substrates permits UBR5 to function in several different signalling pathways and cancers".
   • line 78: "This striking feature allows the positioning of substrate binding sites in close proximity to the catalytic HECT domain in cis or trans, expanding its substrate-recruiting capacities."

Methods section:

• The authors should provide information on how Ubr5 sequence was optimized (line 477).
• The authors should explain why different versions of Ubr5 were used for cryo-EM and activity assays.
• Given the importance of oligomerisation, the authors should explain which fraction of the gel filtration was used for activity assays. Depending on the reversibility of oligomerisation and if oligomerisation impacts activity, the authors should also specify what concentrations these fractions had and/or which concentration they were concentrated to.
• The authors should specify how and at which position cysteine was introduced for labelling of the deltaGG-ubiquitin version.
• The authors should specify which concentrations mass photometry measurements were performed at.
• A description of mass spectrometry measurements is missing.

Results/figures etc:

• Lines 88-91 require more precision: "...highly conserved" - compared to what? Some quantification would help here. "...the length is an average across all species". What is meant by "all species" (all species shown, all metazoans?)?
• Figure 1B shows appears to also show a monomer peak. The authors should label it and comment on it. Can the authors comment on the right shoulder of tetramer peak which was not fitted?
• Figure Legends 1H, 1I, and 1J are missing
• In Figures 1G, 2A and 2B, colour labelling positive/negative is swapped.
• Line 215: "... have observed the formation of free chains". Here, a figure/figure reference is needed.
• Figure 5 C, D, Figure 6: The way models are drawn is very difficult to understand. Maybe the authors could find clearer way to illustrate their hypotheses?

Referees cross-commenting

Reviewer 2 noticed that the manuscript contains a sentence that, in paraphrased form, may have been adopted from a competing manuscript published on Biorxiv some days earlier. According to the conventions of good scientific practice, the competing manuscript should be cited here.

Significance

see above

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Reply to the reviewers

1. General Statements [optional]

We would like to thank the reviewers for taking time in reviewing and commenting on our paper. The comments were very constructive and conscientious, thanks to their expertise in the field. These comments and the revisions would surely make this paper a better and more robust finding in the field.

The comments were about clearer explanations, increasing the quality of the data and additional experiments for a stronger conclusion, all of which we are eager to accomplish. Now we have sorted out the problems and planned the experiments required in the revision, as detailed below.

2. Description of the planned revisions

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

Summary In this manuscript, Komori et al. examined the role of the LRRK2 substrate and regulator Rab29 in the lysosomal stress response. Briefly, in chloroquine (CQ)-treated HEK293 cells the authors observed an apparent LRRK2-independent increased in Rab29 phosphorylation which was accompanied by translocation of Rab29 to lysosomes. Intriguingly, the authors detected a similar increase in Rab29 phosphorylation when Rab29 was tethered to lysosomes in the absence of CQ treatment. Using mass spectrometry, mutagenesis and a phospho-specific anti-body, the authors mapped the CQ-induced phosphorylation site to S185 and demonstrated its independence from LRRK2. Next, the authors found that PKCa was the kinase responsible for S185 phosphorylation and lysosomal translocation of Rab29. Lastly, the authors showed that in addition to PKCa the lysosomal translocation of Rab29 was also regulated by LRRK2. Overall, Komori and colleagues provide interesting new insights into the phosphorylation-dependent regulation of Rab29. However, there are. Number of technical and conception concerns which should be addressed.

Major points 1) Figure 1F: the localization of Rab29 to lysosomes is not convincing at all. The authors should either provide more representative image examples or image the cells at a higher resolution. The authors should also confirm the CQ-induced lysosomal localization of Rab29 in a different cell type (e.g., HEK293).

We will replace Fig 1F pictures with slightly more magnified images with higher resolution. We will also include additional cell types (HEK293, and other cells that are predicted to express endogenous Rab29); Reviewer #2 also raised this point (see Reviewer #2 comment on Significance).

Moreover, the authors should show that prenylation of Rab29 is required for its CQ-induced phosphorylation.

We will test the effect of lovastatin, a HMG-CoA reductase inhibitor that causes the depletion of the prenylation precursor geranylgeranyl diphosphate from cells (Binnington et al., Glycobiology 2016, Gomez et al, J Cell Biol 2019), or 3-PEHPC, a GGTase II specific inhibitor that also causes the inhibition of Rab prenylation (Coxon FP et al, Bone 2005).

2) The rapalog-induced increase in Rab29 phosphorylation in Figure 2D is not convincing since there is at least 2-3-fold more Rab29 in FRB-LAMP1 expressing cells compared to their FRB-FIS1 counterparts. An independent loading control is also missing. This is a key experiment and should be properly controlled and quantified. In addition, can CQ treatment drive 2xFKBP GFP-Rab29 from mitochondria to lysosomes (in the presence of rapalog and FRB-Fis1)?

We will carefully examine another round of rapalog-induced phosphorylation of Rab29, with an independent loading control such as alpha-tubulin. The immunoblot analysis will be made against the intensity of non-p-Rab29. The response to the latter question was described in the section 4 below.

3) Figure 4A-C: Are these stable Rab29 expressing cells? If not, the quantification of "the size of largest lysosome in EACH cell" becomes very problematic. This analysis should be repeated with stable Rab29 variant cells in a background lacking endogenous Rab29. Furthermore, the LAMP1 signal is too dim to see any convincing colocalization (e.g., with WT) or the lack thereof (e.g., in the case of S185D).

The cells shown in Figure 4 are HEK293 cells transiently expressing Rab29, and the issue of quantification was described in the section 3 below. We agree that the signal of LAMP1 was dim, and it turned out that the confocal microscope we used had problems with the sensitivity of the red channels. We will be taking another round of these images with a new confocal microscope.

Lastly, the authors should corroborate their findings with an ultrastructural analysis since the electron microscopy would definitively be more suitable for this type of measurements.

We are planning to obtain electron microscopic images, according to this reviewer’s request. We plan to invite an expert in electron microscopy analysis as a co-author.

4) The lysosomal colocalization of Rab29 in Figure 5C is again not convincing. This analysis needs to be repeated with high resolution imaging.

Again, we will repeat this experiment with a new confocal microscope, with the hope that it would yield better images.

5) The authors need to show the level of LRRK2 depletion (Figure 6). Given the role of LRRK2 in driving lysosomal Rab29 translocation, the importance of the LRRK2 independent pS185 for this process remains unclear.

We will add the level of LRRK2 on its knockdown; we have experienced that LRRK2 knockdown usually occurs with more than 50% efficiency every time. The response to the latter comment was described in the section 3 below.

6) In general, the authors employ an alternative, biochemical assay (e.g., LysoIP) for the lysosomal translocation of Rab29. This would in particular help to clarify the effect of the Rab29 variants and LRRK2 inhibition.

We have previously shown that the overexpressed Rab29 (and LRRK2) is enriched in the lysosomal fraction from CQ-treated cells, which was performed using dextran-coated magnetite (Eguchi et al, PNAS 2018). Using the same biochemical method, we will show the enrichment of endogenous Rab29 in the lysosomal fraction.

Minor points

9) Figure 2C is lacking the control IF staining for mitochondria (to which 2xFKBP-GFP-Rab29 is assumed be recruited upon co-expression with FRB-FIS1).

We will stain the cells with MitoTracker to ensure that anchoring away of 2xFKBP-GFP-Rab29 by FRB-Fis1 results in mitochondrial localization.

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

The data in the manuscript convincingly demonstrates that lysosomal overload by Chloroquine treatment induces Rab29 localisation to the lysosomes and that this membrane association is dependent on PKCalpha-dependent phosphorylation at Ser185.

We have a number of rather minor comments listed below:

Figure 2

The increasing levels of non-phosphorylated Rab29 over the indicated time course of AP21967 treatment in Figure 2B are concerning. First, could you provide an explanation for this clear increase in both non-p-Rab29 and p-Rab29 in the phostag but not the normal gel? Second, could all quantifications of p-Rab29 be made relative to the non-p-Rab29?

We will try another round of rapalog-induced phosphorylation of Rab29, with an independent loading control. The immunoblot analysis will be made against the intensity of non-p-Rab29. Reviewer #1 raised a similar concern on Figure 2D.

Figure 5

To further demonstrate that PKCalpha phosphorylates endogenous Rab29 at Ser185, we recommend reperforming the Go3983/PMA treatment in figure B with the anti-p-Ser185 antibody. It may be sufficient to perform the treatment only at 4 or 8 hours, simply to provide stronger evidence regarding the phosphorylation of endogenous Rab29.

We will give a try, although the anti-phosphorylated protein antibodies that we tried never worked for phos-tag SDS-PAGE. With the conventional western blot, we will be able to try this experiment.

It is not clear whether the activity of PMA in the assay is due to inhibition of PKCalpha. Are the effects ablated by PKCalpha KD

We will test the knockdown of PKCalpha, beta, gamma and delta by siRNAs to further narrow down the effects of PKC-dependent phosphorylation of Rab29.

Reviewer #2 (Significance (Required)):

These cell biology findings are important in the field as both Rab29 and LRRK2 are implicated in the pathogenesis of Parkinson disease. The phosphorilation of Ser185 of Rab29 by PKCalpha is novel and contributes to our understanding of Rab29 and LKRR2 regulation. One limitation of the study is that is conducted in only two cell types quite unrelated to the disease, so how general and disease relevant are the findings it is not clear. Most of the data are solid. There are two experiments whose results are difficult to interpret and a few controls missing. Also a few issues with quantifications, all of which is described in details above and will need to be fixed prior to publication. My expertise for this paper is in the cell biology of lysosomal function.

The issue that only two cell types were analyzed was also raised by reviewer #1, so we will examine additional cell types, especially those that are predicted to express endogenous Rab29. Our responses to other issues raised are described elsewhere. Thank you for these insightful comments.

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

Figure 4A-C: Are these stable Rab29 expressing cells? If not, the quantification of "the size of largest lysosome in EACH cell" becomes very problematic. This analysis should be repeated with stable Rab29 variant cells in a background lacking endogenous Rab29. (Reviewer #1)

As described in the section 2 above, the cells shown in Figure 4 are HEK293 cells transiently expressing Rab29. We are sorry that the description “the size of largest lysosome in each cell” was misleading. As we analyzed only cells overexpressing GFP-Rab29 that were marked with GFP fluorescence, we believe that transient expression should not be a problem. To avoid any misunderstandings, we have described in Figure 4 legends that only lysosomes in Rab29-positive cells (and all cells expressing Rab29) were included in the analysis of the largest lysosome of each cell.

Regarding the effect of endogenous Rab29 in Figure 4 experiments, Reviewer #2 similarly raised the issue on whether Rab29 phosphomimetics are acting as dominant active, preventing lysosomal enlargement. On this point, we have previously reported that knockdown of endogenous Rab29 causes the enhancement of lysosomal enlargement upon CQ treatment (Figure 5I,J of Eguchi et al, PNAS 2018), suggesting that the lysosome-deflating effect by phosphomimetics is a dominant active effect rather than dominant negative suppressing endogenous Rab29. This point is considered significant, and thus has been explained in the results section (page 7, lines 168-171).

Along similar lines: why not all cells in Figure 5E and Figure 5G show Rab29- and LRRK2-positive structures? How do the authors know which of these phenotypes is the prevalent one? (Reviewer #1)

As for the ratio of cells with Rab29- and LRRK2-positive structures, it seems reasonable given that different cells have different levels of exposure to lysosomal stress and that the response is transient and does not occur simultaneously. The ratio of these positive cells may also vary depending on the cell culture conditions. Since Rab29- and LRRK2-positive structures are rarely seen in control cells, we think this would be a meaningful phenotype even if only 20-30% of cells show such structures. The result that the ratio of localization changes is not 100% is now noted in the results section explaining Figure 1G (page 4-5, lines 108-110) where the immunocytochemical data first appears.

Given the role of LRRK2 in driving lysosomal Rab29 translocation, the importance of the LRRK2 independent pS185 for this process remains unclear. (Reviewer #1)

Our data suggested that Rab29 is stabilized on lysosomes only when LRRK2-mediated phosphorylation and S185 phosphorylation both occur on Rab29 molecule (as shown in Figure 7 scheme), so we believe there is no contradiction. We have now described more clearly about this notion at the end of the results section (page 9, lines 235-236).

It is not clear what the authors mean by "lysosomal overload stress". Since mature lysosomal incoming pathways such as autophagy or endocytosis are disrupted by CQ, it is difficult to picture an overload. Maybe rephrasing would help to clarify this. (Reviewer #1)

Chloroquine (CQ) is known as a lysosomotropic agent that accumulates within acidic organelles due to its cationic and amphiphilic nature, causing lysosome overload and osmotic pressure elevation, and this is what we call “lysosomal overload stress”. The well-known effects of CQ to disrupt lysosomal incoming pathways are ultimately caused by the above consequences. Also, we have previously reported that lysosomal recruitment of LRRK2 is caused by CQ but not by bafilomycin A1, the latter being an inducer of lysosomal pH elevation, or by vacuolin-1 that enlarges lysosomes without inducing lysosomal overload/pH elevation (Eguchi et al, PNAS 2018), and further found that not only CQ but also other lysosomotropic agents commonly induced LRRK2 recruitment (Kuwahara et al, Neurobiol Dis 2020). We thus have described the effect of CQ as “overload”. However, it is true that we have not provided a clear explanation for readers, so we have added some notes for lysosomal overload stress in the introduction section (page 3, lines 69-71).

Which cell type is used for the IF analysis in Figure 2C? This information is in general quite sparse. The authors should clearly state the cell type for each experiment/Figure. (Reviewer #1)

We have added cell type information that was missing in several places in the manuscript. We are very sorry for the inconveniences. For clarification, HEK293 cells were used in Figure 2C.

Are the images in figure 1F representative? i.e. does Rab29 always colocalise to such enlarged lysosomes upon CQ treatment and does CQ treatment always drastically alter the cellular distribution of Rab29? (Reviewer #2)

The images in Figure 1F are representative of when Rab29 is recruited, but it is not seen in all cells, and the ratio of recruitment (~80%) is shown in Figure 1G. Reviewer #1 also asked why Rab29 recruitment is not seen in all cells, and we gave the same answer above. It may be reasonable to speculate that different cells have different levels of exposure to lysosomal stress and that the response is transient and does not occur simultaneously. The ratio of these positive cells may also vary depending on the cell culture conditions. For the readers’ clarity, we have added that the ratio of localization change of Rab29 is not 100% and is comparable to that of LRRK2 previously reported (page 4-5, lines 108-110).

Considering that the "forced localisation technique" induces a non-physiological colocalization of non-endogenous Rab29 to lysosomes, it may be an overestimation to conclude just from these data that phosphorylation of Rab29 occurs on the lysosomal surface. This is also quite in contrast with the later finding that phosphorylation by PKCalpha promotes lysosome localization of Rab29. It seems more reasonable to conclude that Rab29 can be phosphorylated when localised at the lysosomes (as opposed to other organelles such as mitochondria). If the authors feel strongly about this point they might need to find a less non-physiological assay. (Reviewer #2)

Yes, it could be an overestimation, and as we do not have better means to conduct a less non-physiological assay, we have modified the description from “occurred on the lysosomal surface” to “could occur on the lysosomal surface” (page 5, line 112 (subtitle) and line 128).

Regarding the comparison with the later finding that phosphorylation by PKCalpha promotes lysosome localization of Rab29, these data (Figure 2 and 5) could be explained with a single speculation: phosphorylation of Rab29 on lysosomal membranes could retain Rab29 on the membranes for a longer time. It is not easy to decipher which comes first, association with membranes or phosphorylation of Rab29, in a physiological assay, but considering reports that show PKCalpha activation happens on membranes (Prevostel et al., J Cell Sci 2000), at least the data favor our conclusion over the idea of PKCalpha phosphorylating Rab29 in the cytoplasm and then promoting lysosomal localization. This point is now clearly described in the discussion (page 10, lines 248-251).

It is not clear how the Rab29 phosphomimetics are acting as dominant active preventing lysosomal enlargement. Authors should speculate or repeat the experiments in absence of endogenous Rab29 to clarify the matter. (Reviewer #2)

A similar concern about the effect of endogenous Rab29 was also raised by Reviewer #1 (see above). We have previously reported that knockdown of endogenous Rab29 causes the enhancement of lysosomal enlargement upon CQ treatment (Figure 5I,J of Eguchi et al, PNAS 2018), suggesting that the lysosome-deflating effect by phosphomimetics is a dominant active effect rather than dominant negative suppressing endogenous Rab29. This point is considered important and thus has been explained in the results section (page 7, lines 168-171).

Overall, there is some missing information regarding repeats for Western blots, such as those in figure 3C, 3D and 3E. Please add indications about repeats in the figure legend or methods. (Reviewer #2)

We have added the repeat information to each figure legend where it was missing. We are very sorry for the inconveniences.

The model in figure 7 however seems to suggest that Rab29 associates to lysosomal membranes independently, and is then stabilised at the membranes by LRRK2 and PKCalpha - a point which is not directly supported by the data. (Reviewer #2)

As noted earlier, we consider that phosphorylation of Rab29 on lysosomal membranes could retain Rab29 on the membranes for a longer time, given the present data and previous reports that phosphorylation of Rab29 is more likely to happen on the lysosomal membrane than in the cytosol. Also, as inhibition of either of the two phosphorylations ends up in disperse Rab29 localization, we have made this figure as a model of what is plausible right now. This explanation is now added in the discussion (page 10, lines 248-251).

English proofreading should be improved: "CQ was treated to HEK293" (page 4), "As we assumed that this phosphorylation is independent of LRRK2" as an opening line (page 5) (Reviewer #2)

Thank you for pointing out these incorrect wordings. They were corrected.

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

In addition, can CQ treatment drive 2xFKBP GFP-Rab29 from mitochondria to lysosomes (in the presence of rapalog and FRB-Fis1)? (Reviewer #1)

We do not think that a comparison between the affinities of FKBP-rapalog-FRB and Rab29-[unknown factor that directs Rab29 to lysosomes] is necessary, as the former has a Kd in the single digit nM range (Banaszynski et al, JACS 2005), whereas the latter (based on estimations from related PPIs) is estimated to be in the μM range, which shows a much weaker affinity than the former (McGrath et al, Small GTPases 2019). Furthermore, even if Rab29 appears to have migrated from mitochondria to lysosomes as a result of this experiment, one cannot rule out the possibility that a small portion of the mitochondrial membrane was incorporated into the lysosomal membrane that was enlarged by CQ treatment.

Molecular weight markes should be provided for all immunoblot experiments. (Reviewer #1)

The immunoblot pictures without molecular weight markers in our paper are all Phos-tag SDS-PAGE blot analyses. Phos-tag SDS-PAGE results in band shifts of phosphorylated proteins, and writing in markers would be misleading. Moreover, previous representative studies heavily using Phos-tag (e.g., Kinoshita et al, Proteomics 2011, Ito et al, Biochemical Journal 2016) also did not show the molecular weight markers. Here we performed phos-tag SDS-PAGE analysis only to find differences in the phosphorylation state of Rab proteins.

The use of the quantification ratio of cells with Rab29-positive lysosomes in figure 1G might be slightly misleading as it does not allow the reader to understand to what extent Rab29 localisation at lysosomes upon CQ treatment. We recommend using a simpler quantification, such as by measuring the average colocalisation of Rab29 and LAMP1 per cell. (Reviewer #2)

For figure 5D and 5F, As with figure 1G, we recommend using a more straightforward and impartial method of quantification such as simply measuring the colocalisation of Rab29 with LAMP1. (Reviewer #2)

Popular colocalization analyses using Pearson’s or Mander’s coefficients would be a good choice if the amounts of Rab29 varied greatly between lysosomes. However, this may not apply in this case; the amount of Rab29 or LRRK2 on each lysosome is considered to saturate quickly and a relatively low amount of them may not be detected on immunofluorescence observations, whereas the probability of finding these structures has been shown to exhibit a moderate sigmoid curve (as seen in Figure 1E or 2H of Eguchi et al., PNAS 2018). Therefore, the amount of Rab29 or LRRK2 could be approximated to a Bernoulli distribution in terms of colocalization with lysosomes, and this is the reason why we chose to quantify “the ratio of cells with Rab29-positive lysosomes”.

We recommend using a more transparent and simple quantification method, such as average size of lysosomes per cell. (Reviewer #2)

As one can see in the inset of Figure 4B, unenlarged lysosomes are unfortunately too small for the quantification of their size, much less tell two small lysosomes apart in our experimental settings and laboratory resources, so we decided to analyze the largest lysosome in each cell as a representative of the cells to minimize measurement errors. This measurement only includes GFP-Rab29 positive cells, and by comparing against CQ-untreated cells we intended to increase the validity of this analysis. This quantification method was also used in our previous report (Eguchi et al, PNAS 2018).

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Referee #2

Evidence, reproducibility and clarity

The data in the manuscript convincingly demonstrates that lysosomal overload by Chloroquine treatment induces Rab29 localisation to the lysosomes and that this membrane association is dependent on PKCalpha-dependent phosphorylation at Ser185.

We have a number of rather minor comments listed below:

Figure 1

• Are the images in figure 1F representative? i.e. does Rab29 always colocalise to such enlarged lysosomes upon CQ treatment and does CQ treatment always drastically alter the cellular distribution of Rab29?
• The use of the quantification ratio of cells with Rab29-positive lysosomes in figure 1G might be slightly misleading as it does not allow the reader to understand to what extent Rab29 localisation at lysosomes upon CQ treatment. We recommend using a simpler quantification, such as by measuring the average colocalisation of Rab29 and LAMP1 per cell.

Figure 2

• Considering that the "forced localisation technique" induces a non-physiological colocalization of non-endogenous Rab29 to lysosomes, it may be an overestimation to conclude just from these data that phosphorylation of Rab29 occurs on the lysosomal surface. This is also quite in contrast with the later finding that phosphorylation by PKCalpha promotes lysosome localization of Rab29. It seems more reasonable to conclude that Rab29 can be phosphorylated when localised at the lysosomes (as opposed to other organelles such as mitochondria). If the authors feel strongly about this point they might need to find a less non-physiological assay.
• The increasing levels of non-phosphorylated Rab29 over the indicated time course of AP21967 treatment in Figure 2B are concerning. First, could you provide an explanation for this clear increase in both non-p-Rab29 and p-Rab29 in the phostag but not the normal gel? Second, could all quantifications of p-Rab29 be made relative to the non-p-Rab29?

Figure 3

• It is not clear how the Rab29 phosphomimetics are acting as dominant active preventing lysosomal enlargement. Authors should speculate or repeat the experiments in absence of endogenous Rab29 to clarify the matter.
• Overall, there is some missing information regarding repeats for Western blots, such as those in figure 3C, 3D and 3E. Please add indications about repeats in the figure legend or methods.

Figure 4

• We recommend using a more transparent and simple quantification method, such as average size of lysosomes per cell.

Figure 5

• To further demonstrate that PKCalpha phosphorylates endogenous Rab29 at Ser185, we recommend reperforming the Go3983/PMA treatment in figure B with the anti-p-Ser185 antibody. It may be sufficient to perform the treatment only at 4 or 8 hours, simply to provide stronger evidence regarding the phosphorylation of endogenous Rab29.
• It is not clear whether the activity of PMA in the assay is due to inhibition of PKCalpha. Are the effects ablated by PKCalpha KD
• For figure 5D and 5F, As with figure 1G, we recommend using a more straightforward and impartial method of quantification such as simply measuring the colocalisation of Rab29 with LAMP1.

Figure 6

• Again, we recommend altering the methods of quantification

Figure 7

• The model in figure 7 however seems to suggest that Rab29 associates to lysosomal membranes independently, and is then stabilised at the membranes by LRRK2 and PKCalpha - a point which is not directly supported by the data.

English proofreading should be improved: "CQ was treated to HEK293" (page 4), "As we assumed that this phosphorylation is independent of LRRK2" as an opening line (page 5),

Significance

These cell biology findings are important in the field as both Rab29 and LRRK2 are implicated in the pathogenesis of Parkinson disease. The phosphorilation of Ser185 of Rab29 by PKCalpha is novel and contributes to our understanding of Rab29 and LKRR2 regulation. One limitation of the study is that is conducted in only two cell types quite unrelated to the disease, so how general and disease relevant are the findings it is not clear. Most of the data are solid. There are two experiments whose results are difficult to interpret and a few controls missing. Also a few issues with quantifications, all of which is described in details above and will need to be fixed prior to publication. My expertise for this paper is in the cell biology of lysosomal function.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this manuscript, Komori et al. examined the role of the LRRK2 substrate and regulator Rab29 in the lysosomal stress response. Briefly, in chloroquine (CQ)-treated HEK293 cells the authors observed an apparent LRRK2-independent increased in Rab29 phosphorylation which was accompanied by translocation of Rab29 to lysosomes. Intriguingly, the authors detected a similar increase in Rab29 phosphorylation when Rab29 was tethered to lysosomes in the absence of CQ treatment. Using mass spectrometry, mutagenesis and a phospho-specific anti-body, the authors mapped the CQ-induced phosphorylation site to S185 and demonstrated its independence from LRRK2. Next, the authors found that PKCa was the kinase responsible for S185 phosphorylation and lysosomal translocation of Rab29. Lastly, the authors showed that in addition to PKCa the lysosomal translocation of Rab29 was also regulated by LRRK2. Overall, Komori and colleagues provide interesting new insights into the phosphorylation-dependent regulation of Rab29. However, there are. Number of technical and conception concerns which should be addressed.

Major points

1. Figure 1F: the localization of Rab29 to lysosomes is not convincing at all. The authors should either provide more representative image examples or image the cells at a higher resolution. The authors should also confirm the CQ-induced lysosomal localization of Rab29 in a different cell type (e.g., HEK293). Moreover, the authors should show that prenylation of Rab29 is required for its CQ-induced phosphorylation.
2. The rapalog-induced increase in Rab29 phosphorylation in Figure 2D is not convincing since there is at least 2-3-fold more Rab29 in FRB-LAMP1 expressing cells compared to their FRB-FIS1 counterparts. An independent loading control is also missing. This is a key experiment and should be properly controlled and quantified. In addition, can CQ treatment drive 2xFKBP GFP-Rab29 from mitochondria to lysosomes (in the presence of rapalog and FRB-Fis1)?
3. Figure 4A-C: Are these stable Rab29 expressing cells? If not, the quantification of "the size of largest lysosome in EACH cell" becomes very problematic. This analysis should be repeated with stable Rab29 variant cells in a background lacking endogenous Rab29. Furthermore, the LAMP1 signal is too dim to see any convincing colocalization (e.g., with WT) or the lack thereof (e.g., in the case of S185D). Lastly, the authors should corroborate their findings with an ultrastructural analysis since the electron microscopy would definitively be more suitable for this type of measurements.
4. The lysosomal colocalization of Rab29 in Figure 5C is again not convincing. This analysis needs to be repeated with high resolution imaging. Along similar lines: why not all cells in Figure 5E and Figure 5G show Rab29- and LRRK2-positive structures? How do the authors know which of these phenotypes is the prevalent one?
5. The authors need to show the level of LRRK2 depletion (Figure 6). Given the role of LRRK2 in driving lysosomal Rab29 translocation, the importance of the LRRK2 independent pS185 for this process remains unclear.
6. In general, the authors employ an alternative, biochemical assay (e.g., LysoIP) for the lysosomal translocation of Rab29. This would in particular help to clarify the effect of the Rab29 variants and LRRK2 inhibition.

Minor points

1. It is not clear what the authors mean by "lysosomal overload stress". Since mature lysosomal incoming pathways such as autophagy or endocytosis are disrupted by CQ, it is difficult to picture an overload. Maybe rephrasing would help to clarify this.
2. Which cell type is used for the IF analysis in Figure 2C? This information is in general quite sparse. The authors should clearly state the cell type for each experiment/Figure.
3. Figure 2C is lacking the control IF staining for mitochondria (to which 2xFKBP-GFP-Rab29 is assumed be recruited upon co-expression with FRB-FIS1).
4. Molecular weight markes should be provided for all immunoblot experiments.

Significance

Please see above.

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Reply to the reviewers

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

Basier and Nurse revisit the fundamental question of how the rates of RNA and protein synthesis scale with cell size. The strong null hypothesis is that synthesis scales linearly with cell size: cells that are twice as big should make stuff twice as fast. This hypothesis has been tested many times, in many systems, using many approaches over the past century and, in general, the null hypothesis has been sustained. However, there have been many examples of evidence for more complicated synthetic patterns. Whether these results indicate that biosynthesis rates vary across the cell cycle, or in response to other factors, in addition to increasing with cell size, or whether observed deviations from the predictions of the null hypothesis has been due to artifacts of cell synchronization and labeling, is thus an open, interesting and, because biosynthesis rates have critical implications in cellular function and metabolic robustness, important question.

The authors address the question in fission yeast using metabolic pulse labeling with a ribonucleoside or amino acid analog in asynchronous cells and single cell analysis to directly compare incorporation levels with cell size and cell cycle stage. The experiments are well designed, well executed and well controlled. Furthermore, the data is well presented and appropriately interpreted. In particular, the presentation of the size-v.-label data in Figures 2A and D, with the averages and variances in 2B and E and the normalized data in 2C and F are easy understand and interpret. It is thus notable that the size-v.-label data for the longer (cdc22-22) cells is omitted in favor of just the average (2H,J) and normalized (2I,K) data. This size-v.-label data should be added to Figure 2.

We added two panels to the Figure supplementary 2 showing the requested data, the size-v.-global translation (S2E) and size-v.-global transcription (S2F).

The authors should also explicitly state how they chose 15 µm as the inflection point in 2H; 16-17 µm seems like it would give a horizontal plateau, which would better fit their saturation explanation.

This comment relates to the second comment of reviewer 4, see below for the detailed answer.

The authors measure DNA content with a DNA-binding dye, the signal from which should linearly scale with DNA content. However, instead of reporting and analyzing total signal from the DNA-binding dye (or better yet, total signal in the nucleus, which they could do, having segmented the nucleus in their images), they report max signal. Using max signal is complicated because, as cells and thus nuclei increase in size the concentration of DNA and thus the max (but not total) DNA-binding-dye signal in in the nucleus decreases, requiring two-dimensional dye/size analysis (such as shown in Figure 3B) to distinguish G1 and G2 cells. The authors should use the more straight forward measure of total nuclear DNA-binding dye signal, or explicitly explain why they can't or prefer not to do so.

The total fluorescence intensity signal of the DNA-binding dye is noisy because we had to use a low concentration of the dye. This was necessary as it allows a clearer distinction between cells with a one 1C DNA content and cells with a 2C DNA content that higher concentrations did not. The maximum signal per cell-v.-cell length produces distinct populations of cells in G1, or G2/M phase (see Figure 3H, and Figure 4B), and populations identified in this way have the distributions of total fluorescence intensity expected from cells in G1 and G2 or M phase (see Figure 3I and Figure S4D). We added one extra panel to Supplementary Figure 4 showing the distributions of the total fluorescence intensity signal of the DNA-binding dye for the G1, S, and G2 or M populations (S4D) for comparison.

The authors should state in figure legends the strain numbers used for all experiments.

We have modified all the figure legends to include the strain numbers.

They should also cite the source of all the constituent parts (e.g. hENT1, hsvTK, EGFP-pcn1, and synCut3-mCherry) of their strains.

The missing reference for the source of hENT1 and hsvTK (Sivakumar et al. 2004) has been added, the references for EGFP-pcn1 (Meister et al., 2003) and synCut3-mCherry (Patterson et al., 2021) were already present.

CROSS-CONSULTATION COMMENTS My colleagues make constructive points. I agree with all of them, although I am less concerned about the use of cdc2-22 and CCP∆ to alter cell length and cell cycle distribution. Although these mutations alter CDK specific activity (and thus length and distribution) and could alter specific patterns of translation, the fact that they double at normal rates makes it seem unlikely that they could be significantly changing bulk synthesis rates.

Reviewer #1 (Significance (Required)):

As noted above, this work addresses an open, interesting and important question. Moreover it provides useful data in a specific system and a useful example of a general experimental approach to the problem. However, it does not settle the question of how biosynthesis scales with size, even in the specific case of fission yeast. In particular, it shows that protein synthesis plateaus just above normal cell size, whereas RNA synthesis scales up to twice normal cell size. This observation is striking, because there is no obvious mechanism that would (and the authors offer no suggestion of how to) explain how protein synthesis could be limited if RNA synthesis is not. Therefore, the strength of the paper is that it identifies an intriguing phenomena and its limitation is that it does not provide any testable hypotheses to explain that phenomena.

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

Summary: Basier and Nurse investigate how "cell size, the amount of DNA, and cell cycle events affect the global cellular production of proteins and RNA molecules". Both transcription and translation, driving the production of biomass, have been shown to increase as a function of cell size in various systems. However, whilst cell size generally correlates with cell cycle progression there are inconsistent results in the literature if global cellular translation and transcription is affected by cell cycle state. They argue that this might be due to perturbations induced by different synchronisation methods used in the various studies.

Therefore, in this study, to avoid potential perturbation from synchronisation methods, they developed a system that allows to assay unperturbed exponentially growing populations of fission yeast cells. The assay is based on single-(fixed)cell measurements of cell size, cell cycle stage, and the levels of global cellular translation and transcription. This allows them to correlate cell cycle state, cell size and global cellular translation and transcription levels at the single cell level under unperturbed conditions.

Their results show that translation and transcription steadily increase with cell size, but that the rate of translation, but not transcription, becomes rapidly restricted when cells become larger than wild type dividing cells. This suggests that it is unlikely that the synthesis of RNA is the limiting factor for translation rate in large cells. In addition, their data indicates that translation scales with size, but that the rate increases faster at late S-phase/early G2 and even faster in early in mitosis before decreasing in mitosis and return to interphase. Transcription, on the other hand, increases as a combination of size and the amount of DNA. Overall, this suggests that cell cycle control affects global cellular translation and transcription, which is in line with some studies, but not others. As far as I can tell the assays and data analysis are robust and the data supports the general conclusions.

Major comments I agree that inconsistent results published on this topic might be due to perturbations induced by different synchronisation methods used in the various studies. However, but much less emphasised in the paper, it also likely depends on the model system used. For example, in budding yeast there is strong evidence for gene expression homeostasis, i.e. gene expression increases as a function of size, independent of gene copy number. Do the authors believe this is a budding yeast specific phenomenon or is this a consequence of specific synchronisation methods used in budding yeast?

Gene expression homeostasis has been suggested for budding yeast, but in contrast recent work in budding yeast also suggests that gene expression increases with the genome copy number and therefore the gene copy number in addition to cell size (Swaffer et al., 2022 – currently on bioRxiv). The differences that have been reported might be due to perturbations such as synchronisation methods as well as differences between yeast species.

Whether growth rate increases linearly or exponentially has been the topic of decade long debates. Their data indicates that the translation rate increases faster at late S-phase/early G2 and even faster early in mitosis before decreasing in mitosis and return to interphase, 'resetting' the growth rate. This suggest an exponential, rather than linear, increase in biomass (i.e. growth rate?), but this is not explicitly pointed out. It would be good to get the authors opinion on this in the discussion.

Assuming that protein degradation remains constant throughout growth, the increase of translation with cell size suggests that the growth rate increases as cells grow in size, possibly exponentially. In addition, our data showing that the translation rate increases from G1 to G2 for the same cell size, suggests that for cells of a given size the growth rate is faster in G2 than in G1. Thus, growth could be basically exponential but the speed of increase accelerates at the transition between S and G2, and early in mitosis, slowing down later in mitosis. We added the following sentence to the discussion section “Global transcription and translation increase with cell size possibly exponentially, but the changes in global translation during transitions through cell cycle stages suggest that the speed of growth is modulated by cell cycle progression, increasing between S and G2, and early in mitosis, and slowing down later in mitosis.”.

The authors state that their approach has allowed them to determine how cellular changes are arising from progression through the cell cycle. However, they use fixed cells, rather than live cell imaging, so can't claim to have established changes during cell cycle progression, but only a correlation with cell cycle state/phase. Whilst this could be used as a proxy for progression it should be clearly stated in the abstract and elsewhere to prevent confusion. I for one, based on the abstract, thought they developed a live cell imaging strategy to look at this.

We have modified the abstract to reflect the fact that the cells were fixed in our assays (line 36).

In reference to the Stonyte, et al., study, in addition to different conditions (temperature shift and isoleucine medium), why do the authors think their findings are different? Is it the lack of correlation to cell size in the Stonyte paper or something else? For example, would using different growth conditions (as in the Stonyte paper). where fission yeast cells spend more time in G1, be used instead of the CCP mutant? Can the authors exclude that the lack of G1-S/cyclin-CDKs is not at the basis of a lower rate of translation in G1 and S phase cells? Either these experiments should be carried out or this should be discussed in more detail.

In the study carried out by Stonyte et al., the relative translation rate per cell (a measurement related to our measurement of translation normalised per unit of length) of wild type fission yeast cells grown asynchronously in isoleucine minimal medium is constant between the G1 and the S phase cell populations, and is higher in the G2 population compared to the S phase population (Figure 2D of Stonyte et al., 2018). This is consistent with the lack of increase that we observe for a given cell size from G1 to G2, and the increase we observe from S to G2 in Figure 3K. In the same figure, Stonyte at al., find no difference between the G2 and the M-G1 populations but are not able to distinguish cells at different stages of mitosis or in early G1. Our study suggests that translation increases early in mitosis before decreasing after anaphase A, thus in the Stonyte et al study, pooling all stages of mitosis and early G1 cells might mask the dynamics of what is happening during mitosis. The lack of G1-S/cyclin-CDK could be the basis for the lower rate of translation in G1 and S-phase. We discuss this further in a reply to the first question of the significance part of reviewer 2 and have added a section to the discussion of the paper (see below for details).

If the signal to noise signal is reduced by 20 minutes EU incubation (rather than 10 minutes) why wasn't it used in all experiments?

To measure RNA production as closed as possible to the instantaneous rate of RNA synthesis, we sought to use the shortest pulse possible. We did this because the half-lives of some RNA species are short, in particular, the half-life of the pool of mRNA has been reported to be around 13.1 minutes in budding yeast (Chan et al., 2017). In longer pulses, some RNA molecules that have been synthesised after addition of EU will therefore have been degraded before cells are fixed, producing a measurement that underestimates the rate of RNA synthesis. We chose to incubate cells for 10 minutes as we estimated it to be the shortest time generating a signal to noise ration above 1 (Figure 1F). The one exception to this was with the pulsing of the CCP∆ EGFP-pcn1 hENT1 hsvTK mutant cells which incorporates less EU during the same time frame so we incubated this strain for 20 minutes to generate enough signal to be quantifiable (see line 237, “we assayed CCP∆ EGFP-pcn1 hENT1 hsvTK cells for global transcription using a 20-minute EU incubation to compensate for their lower signal production”).

And the conclusion that the increase in transcription is not showing any discontinuities, are they referring to the triplicates in the supplementary figure 2?

We think there might be a misunderstanding. We conclude that the increase in transcription shows no discontinuity because the median transcription increases steadily with cell length in Figure 2E. We have added “since global transcription increases smoothly with cell length (Figure 2E)” to clarify the text.

Minor comments Lines 168-169: should be Figure 2F, S2C, S2D rather than Figure 2C, S2A, S2B.

The figure numbers have been corrected in the manuscript.

Line 179: doubling time instead of growth rate?

The mention of “growth rate” has been changed to “doubling time” in the manuscript.

Lines 184-186: There is an overall trend of slight decrease in transcription per length in cdc25-22 cells but a slight increase in wild-type cells. How does this differ to wild-type cells? Are these non-significant changes and could these be attributed to the low signal to noise ratio?

These changes may be due to the low signal to noise ratio in the cdc25-22 transcription assay. We have added “The decrease with cell length in transcription that we observe in the cdc25-22 hENT1 hsvTK (Figure 2K) cells but not in the hENT1 hsvTK cells (Figure 2F) may be due to the low signal to noise ratio”.

There is no cell size that is specific to S phase, it falls within the range of G1 and G2 cells. Since this strain has a variable onset of S phase, the phase durations could differ. Therefore, could time spent in each phase affect the translation rate (live cell imaging, i.e. progression, could address this, but not fix cell correlation)?

It is possible that the phase duration of G1 and G2 could differ from one cell to another. There is no evidence that the length of S-phase varies in these cells. It would be interesting to measure how the phase length influences translation, but our techniques do not allow for the measurement of global translation in living cells.

The data reflects translation/transcription in single cells at a specific cell cycle phase, not during the transition between cell cycle phases. Therefore, it would be more appropriate to only use G1, S, G2 and M rather than S/G2 transition or early G2.

Our data represents cells at fixed cell cycle phases and we do not monitor the transition themselves directly. However, the discontinuity in signal for cells of the same size in consecutive stages of the cell cycle (for instance the discontinuity in translation between S and G2 cells of the same size in Figure 3J) is indicative that the transition between the two cell cycle phases is a consequence of a rate change.

In figure 4C, there is a decrease in global transcription after 13 um (black line showing all cells), which they don't see in cdc25-22 mutants. Their conclusion that global transcription is constantly increasing with cell size is based on cdc-25 cells but the experiment in CCP mutant cells shows a decrease in the median of transcription. Are there replicates for these experiments as in figure 2 and supplementary figure S2? Maybe an average trend can be plotted too? Apart from the first set of experiments (figure 2 and supplementary figure 2), they don't show replicates for other strains. Maybe they can include another graph as in figure 3D and 3K of average replicate values?

The apparent decrease in transcription on Figure 4C in long cells is seen in only one length bin (13.5 µm), which has a smaller number of cells compared to the ones directly before (89 cells, compared to 216 cells for the 12.5 µm bin and 316 cells for the 11.5 µm bin). This might have resulted in a higher variability in the measurement of the population median. We do not see the same decrease at 13.5 µm in the wild type (Fig 5G), the cdc25-22 mutant (Fig 2J), or the CCP∆ strain (Fig S4B) so on balance we favour the interpretation that the decrease observed in the longer length bin of Figure 3J is due to variability caused by the lower number of cells in that bin.

CROSS-CONSULTATION COMMENTS I believe that since the whole premise of this study is that by using unperturbed conditions their findings are different from previously published work they should either clearly point out that this difference might be due to using mutations affecting CDK activity or carry out an experiment in media that induces a G1 population. CDK has been strongly implicated in promoting translation. Using a strain that lacks the G1 and S cyclin CDKs or compromised M-CDK is therefore likely to have an effect on translation, which could be at the basis of the increase in translation during the G2 (and S) phase of the cell cycle.

This is addressed in the next comment.

Reviewer #2 (Significance (Required)):

As far as I can tell the assays and data analysis are robust and the data supports the general conclusions. However, whilst the cells are assessed in unperturbed conditions, they do use CDK mutants and the cdc25ts mutant to establsih gene expression during the different phases of the cell cycle, which could affect translation/transcription rates. This should either be clearly pointed out or complemented with an experiment where WT cells are grown in conditions that induces distinct G1-S-G2 populations of cells.

The cell cycle stage and CDK activity are intrinsically linked. CDK activity defines the cell cycle stage so that an increase in CDK activity through the cell cycle is responsible for cells progressing through G1, S, G2, and mitosis (Coudreuse and Nurse, 2010, Swaffer et al., 2016). Nutritional conditions that induce a G1 also rely on repression of CDK activity through increased production of the Rum1 inhibitor (Rubio et al., 2018) to generate a G1 population. Therefore, uncoupling CDK activity from the cell cycle would not be possible in an unperturbed cell population. We have added the following paragraph to the discussion to address the comment “The cell cycle stage of a cell and the activity of its CDK molecules are intrinsically linked since CDK activity defines the cell cycle stage of a cell. CDK activity increases through the cell cycle and is responsible for cells progressing through G1, S, G2, and mitosis [44,53] so that an unperturbed asynchronous population of cells in G1 is achieved by a low CDK activity. Thus our results reflect changes happening through the cell cycle as the CDK regulation network undergoes modifications, and an unperturbed cell cycle therefore cannot be uncoupled from CDK activity.”.

Overall, the work presented suggests that cell cycle control affects global cellular translation and transcription, which is in line with some studies, but not others. Whilst the study falls short of testing/establishing the (potential) mechanisms involved, these are important findings, which can be used to guide new studies into how the production of biomass is controlled as cells proceed through the cell cycle.

The cell size field, which is considerable and growing, will be interested in this work.

I have expertise in cell cycle control and genome stability, with a focus on the G1-to-S transition and cell cycle checkpoints during interphase.

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

Summary Basier and Nurse use fission yeast as a model system to investigate how transcription and translation are coupled to cell-cycle progression. They use metabolic labeling in exponentially growing cells and analyze single cells by microscopy. They find that translation scales with size and increases at S/G2 and early mitosis while transcription increases with both size and the amount of DNA. They suggest that changes in CDK activity regulate changes in global translation rates.

Major comments: 1) The paper addresses a much-disputed question in the field. The approach makes the most of the fission-yeast model system and the experiments are beautifully performed. The conclusions are well supported by the data. The experiments are replicated adequately and the statistical analyses are appropriate.

2) The use of cdc25 and in particular the cig1Δ cig2Δ puc1Δ mutants to manipulate cell size is not without challenges when monitoring translation rates. A number of reports in different model organisms suggest that CDK activity can regulate translation. Work from the Nurse lab identified translation factors as CDK substrates (Swaffer et al, 2016), RNApolIII activity and thus tRNA levels are regulated in the cell cycle by CDK in budding yeast (Herrera et al, 2018), phosphorylation of the ribosomal protein RPL12 by CDK1 is required for translation of at least some proteins in mitosis in human cells (Imami et al, 2018), as is phosphorylation of DENR (Clemm von Hohenberg et al, 2022). The authors also suggest that changes in CDK activity might be responsible for the observed changes in global translation rates. It is important to consider whether using mutants impinging on CDK activity might lead to under- or overestimating cell-cycle dependent translation. The authors should either discuss this issue and tune down the hypothesis that CDK activity regulates changes in global translation rates, or use another approach to address the issue. One could use a replication mutant such as cdc17 or cdc20 to alter cell size without interfering with CDK activity. These experiments would strengthen the conclusions and might support the idea that CDK activity regulates changes in global translation rates. References Clemm von Hohenberg K, Müller S, Schleich S, Meister M, Bohlen J, Hofmann TG, Teleman AA (2022) Cyclin B/CDK1 and Cyclin A/CDK2 phosphorylate DENR to promote mitotic protein translation and faithful cell division. Nat Commun 13: 668 Herrera MC, Chymkowitch P, Robertson JM, Eriksson J, Bøe SO, Alseth I, Enserink JM (2018) Cdk1 gates cell cycle-dependent tRNA synthesis by regulating RNA polymerase III activity. Nucleic Acids Res 46: 11698-11711 Imami K, Milek M, Bogdanow B, Yasuda T, Kastelic N, Zauber H, Ishihama Y, Landthaler M, Selbach M (2018) Phosphorylation of the Ribosomal Protein RPL12/uL11 Affects Translation during Mitosis. Mol Cell 72: 84-98 e89 Swaffer MP, Jones AW, Flynn HR, Snijders AP, Nurse P (2016) CDK Substrate Phosphorylation and Ordering the Cell Cycle. Cell 167: 1750-1761 e1716

As discussed above in the reply to reviewer 2, the cell cycle stage and CDK activity are intrinsically linked, CDK activity defines the cell cycle stage so that an increase in CDK activity through the cell cycle is responsible for cells progressing through G1, S, G2, and mitosis (Coudreuse and Nurse, 2010, Swaffer et al., 2016). Therefore, uncoupling CDK activity from the cell cycle is not possible in an unperturbed population. Temperature sensitive mutants of cdc20 (Ramirez et al., 2015, Win et al., 2002) and cdc17 (Jimenez et al., 1992) cause loss of viability when cells are shifted to the restrictive temperature so it cannot be assumed that they are in unperturbed conditions which makes results hard to interpret. It should be noted as far as possible in these experiments we have tried to avoid perturbations. In addition, the fraction of cells permeabilised in our assay decreases significantly when cells are grown above 30 °C, making it difficult to assay such temperature shifts.

Minor comments: 1) The figures are beautifully presented, easy to understand and the cartoons present the experimental strategies very clearly.

2) A major feature of the approach is that translation and transcription are monitored in exponentially growing cells, which are not exposed to any stress such as cell-cycle synchronization. However, one could argue that the analogues used for labeling impose some kind of stress, even if this is not very likely at the labeling times employed. A simple control experiment where the growth rates of labeled and unlabeled cells are compared would strengthen the claim that these are indeed happily growing cells.

It is possible that incubating cells with the analogues could impose some kind of stress on the cell although that could be said about almost any experimental procedure. We have added two supplementary figures with the suggested experiments, showing that incubating cells with EU has little or no impact on their doubling time (we see at most a 2.4 % increase in doubling time in hENT1 hsvTK cells incubated with 20 µM EU, Figure S1I) and that incubating cells with HPG has little impact on their doubling time (we see a 8.6 % increase in doubling time in wild type cells incubated with 10 µM HPG, Figure S1H). Considering the small impact of analogue incubation on the doubling time of the population, and the fact that cells are only exposed to the analogue for a short time in our assays (compared to continuous growth in the presence of the analogue in the growth curves presented in Figure S1H and I), we conclude that the stress imposed is low.

3) Please comment why the length of the EU labeling differs from figure to figure. In fig 2C, S2C and S2D the labeling on the y axes states 10 min, in Fig 4C it says 20 min.

Please refer to the reply to reviewer 2 on the same topic.

4) Lines 118-119 "The pulse signal was five times the background signal." Figure S2A,B show large variation in signal intensity after 5 min labelling. It is not clear how the pulse signal was estimated to be five times the background signal.

We have added two panels for the supplementary figure 2 showing how the signal to noise ratio was computed for the HPG assay after 5 minutes of incubation (Figure S2G) and for the EU assay after 10 minutes of incubation (Figure S2H).

5) In Fig S4C transcription is up by ca 60 % from G1 to G2, while in Fig 4D transcription is up by ca 25-30%, also from G1 to G2. The only difference I can see is the use of PCNA-GFP. Please comment what the reason might be.

In Figure 4D, transcription is up 33 % from G1 to G2 and in Figure S4C, transcription is up 62 % from the 1C to the 2C population. It is possible that the EGFP-pcn1 strain might have a small growth defect which could possibly explain its lower signal production, the slower growth rate might mean that the concentration of RNA polymerase could be lower in this strain and the dynamic equilibrium model predicts that this would results in a smaller increase from G1 to G2 compared to cells with a higher concentration of RNA polymerase. But obviously this is speculative.

6) Fig 1 B images of unlabeled control cells should also be shown.

We have added 2 panels to the supplementary figure 1 showing the background controls in which cells are fixed immediately after addition of the analogue for the HPG assay (Figure S1F) and for the EU assay (Figure S1G).

7) Lines 156 "to investigate how global cellular translation and transcription are affected by cell size, and by progression through the cell cycle" should be amended. Throughout the description of data in figure 2 binucleated and septated cells were excluded from the analyses, meaning that the data only represent cells in G2. The text should make this clear.

"to investigate how global cellular translation and transcription are affected by cell size, and by progression through the cell cycle" has been changed to "to investigate how global cellular translation and transcription are affected by cell size and by progression through G2" to reflect the fact that binucleated and septated cells are excluded from the analysis on this figure.

8) Lines 241-243 "the S-phase subpopulation was found to have an intermediary global transcription value between the G1 and G2/M subpopulations of around 20-25 %." And Lines 310-313 "the rate of transcription is increased in cells undergoing S-phase by 20 % and is 35 % higher in G2 cells which have completed S-phase, indicating that DNA content is limiting the global rate of transcription." It is unclear what the percentage values refer to and which populations exactly are being compared.

"the S-phase subpopulation was found to have an intermediary global transcription value between the G1 and G2/M subpopulations of around 20-25 %" has been changed to “the S-phase subpopulation was found to have an intermediary global transcription value between the G1 and G2/M subpopulations with an increase of around 20-25 % compared to the G1 subpopulation” and “the rate of transcription is increased in cells undergoing S-phase by 20 % and is 35 % higher in G2 cells which have completed S-phase, indicating that DNA content is limiting the global rate of transcription” has been changed to “the rate of transcription is increased in cells undergoing S-phase by 20 % compared to G1 cells and is 35 % higher in G2 cells which have completed S-phase compared to G1 cells, indicating that DNA content is limiting the global rate of transcription”. These changes hopefully will clarify what populations comparisons the percentage values are referring to.

9) Line 85 "Asynchronous cultures ... have not detected" rephrase; change detected to displayed or similar.

“detected” has been changed to “displayed”

10) Line 243 Figure 4J, K should read Figure 4C, D.

“Figure 4j, K” has been changed to “Figure 4D, C”

CROSS-CONSULTATION COMMENTS

I also agree with the comments made by the colleagues. As for the use of the cyclin and cdc25 mutants: I agree with Reviewer #1 that it is unlikely that bulk synthesis rates are conisedarably different, since these strains are going at more or lass normal rates. However, I also agree with reviewer #2 that these mutants cannot be considered as unperturbed conditions. I suspect subtle regulation and in particular cell-cycle dependent regulation might well be lost. At the very least the focus of the interpretation should be on translation/transcription as a function of size, rather than in terms of cell-cycle regulation.

Reviewer #3 (Significance (Required)):

Basier and Nurse address a long-standing question in the cell-cycle field, namely how/whether transcription and translation are coupled to cell-cycle progression. This is technically challenging to address, and many previous studies were hampered by the necessity to synchronize the cells in the cell cycle. The approach of this study of using metabolic labeling in non-synchronized cells is not novel in itself. However, the analysis by microscopy is superior to previous flow-cytometry based strategies in that it allows the use of cell-cycle markers and thereby precise identification of cells in each cell-cycle phase. In addition, it allows accurate measurements of cell size and thus addressing questions of correlations between cell size and transcription / translation rates. A further strength of the study design is that they investigate both transcription and translation in parallel. The authors very nicely review the existing literature and point out the likely reasons for conflicting conclusions (synchronization methods, choice of model system). The advantages of their approach, such as single-cell analyses in non-synchronized cells and the use of cell-cycle markers make their conclusions less likely to be flawed and thus represent an important advance in the field. These findings are of interest for researchers working on the cell-cycle field and on the translation field. There have been significant technical advances in the translation field in recent years, allowing studying not only global translation but also translation of specific mRNAs. I expect that the old questions of coupling cell cycle and cell growth will be revisited also by others, exploiting these new approaches. My field of expertise extends to the cell-cycle field and the regulation of translation and the use of fission yeast.

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

Summary Single cell measurements (flow cytometry and imaging) from unperturbed cells are obtained to investigate scaling of transcription and translation in fission yeast. A key finding is that translation and transcription are somewhat differentially responding to changes in cell size and cell cycle. Perhaps the most central finding of this manuscript is that transcription is not a limiting factor to translation and suggests that transcription is not limiting growth (increase in biomass).

Major comments: What I like in this manuscript is that the translation and transcription measurements have been carefully checked to reflect the initial rates before the HPG and EU signals lose their linearity. More generally, experiments have been conducted with appropriate controls, and the analysis of unperturbed cells in each cell cycle phase is likely to be highly relevant for resolving some of the controversies in the field. Most claims and the conclusions are well supported by the data. Although it is encouraging that the results for translation match the single cell mass measurements in mammalian cells (e.g., ref 18), I would have liked to see some more discussion about the potential caveats of the performed analyses such as the low signal to noise ratio in EU incorporation and other potential technical issues, which might have confounded the results. As an example, looking at Figs 1B and E, most of the protein and RNA synthesis signal is nuclear localized. Is this due to nucleolar staining and incorporation of the labels into nascent ribosomes? Yet the manuscript mentions that roughly half of RNA is for rRNA and for ribosomal proteins the fraction of HPG incorporation might be even lower. This statement does not sound entirely consistent with the experimental images shown in Fig 1. Please clarify.

We had initially performed modelling to estimate the proportion of rRNA in transcription but after reconsideration we agree that is difficult to assess whether the special pattern we observe is consistent with the statement that roughly half of the nascent RNA is rRNA. There is signal in the cytoplasm indicating that within the pulse time some RNA are exported from the nucleus, thus the localisation of the RNA signal is not necessarily an accurate indication of the fractions of the different RNA types in global transcription. We have removed the statement “Although the precise fractions of the different types of RNA in global transcription have not been fully characterised, recent work indicated that only half of the newly synthesised RNA consists of ribosomal RNA molecules, suggesting that a significant portion of transcription is dedicated to the production of messenger and other RNA molecules [27].” It cannot be concluded that most of the protein synthesis is nuclear located in Figure 1B. As mentioned in the text we cannot differentiate between proteins being synthesised in the nucleus and proteins being rapidly imported, we also cannot say what fraction of the proteins synthesised are related to ribosome biogenesis.

A curious thing that has been glossed over is that the transcription and translation seem not to be completely linear but to display opposite patterns (translation slightly reducing, transcription slightly overshooting with cell size compared to a linear model). It remains possible that this could be experimental noise and a visual pattern that is not real, but it could also be relevant for growth control. For example, my interpretation from Fig. 2B is that the signal is not linear and starts to saturate around 10.5 um cell length as seen from the upper IQR. Related to this, I think it is oversimplification to force the data to appear as a discontinuous linear trend by splitting the data in 2H into two segments. Such a treatment will obviously match the data better than a single linear regression, but perhaps some nonlinear model would be actually much more accurate, unless you can point out some kind of regulatory event at the intersection of these two linear segments. In my opinion the current data looks more like a typical (logarithmic) growth curve of the cell population reaching saturation. Please comment.

We agree that fitting two linear regressions for cells shorter and longer than 15 µm is in Figure 2H and 2I was an oversimplification which could result in a false discontinuity in the data. This echoes a comment from reviewer 1 pointing out that 15 µm might not be the length at which the transition occurs. We have removed the linear regressions and added a locally estimated scatterplot smoothing (LOESS) function which capture the nonlinear transition between the increase of translation with size and the saturation, and we have changed the cell length at the estimated saturation from 18 to 19 µm in the text to better reflect the trend.

The main conclusion presented in the abstract is that scaling in transcription may result from dynamic equilibrium between RNA polymerases and available DNA template. This is a bit of speculative part, which I was not too fond of. The dynamic equilibrium idea has been suggested also elsewhere (refs 47) and is not well developed in this manuscript. There is a lack of mechanistic understanding and no formal (mathematical) model to support this idea. For example, global transcription increases much less (1.3-1.4x) than expected based on the increase in DNA content from G1 to G2 (2x). Is this expected based on the dynamic equilibrium model?

The dynamic equilibrium model has been proposed and developed by Swaffer et al. (2022 – currently on bioRxiv) based on mass action kinetics describing the interaction between RNA polymerases and DNA. The model predicts that transcription increases with cell size and with the amount of DNA. With this model, the increase in transcription with DNA for a given cell size is also a function of cell size. Smaller cells are predicted to have a smaller relative increase in transcription from 1C to 2C DNA content than larger cells. This implies that depending on the cell size to DNA ratio of a cell, the span increase in transcription produced by a doubling in the amount of DNA goes from a small increase (at small cell size to DNA ratio) to a doubling (at large cell size to DNA ratio). Thus, in our view the 1.3-1.4x increase in transcription we observe from G1 to G2 is consistent with the dynamic equilibrium model.

I am somewhat concerned about the interpretation of the S phase data in the global transcription measurement. The quantification in Fig. 4D shows S phase being intermediate between G1 and G2. Yet, when you look at the data in Fig. 4C, the S phase median is clearly discontinuous, with higher transcription in smaller S cells. I believe this could affect the normalized data in Fig. 4D and result in the apparent increase in transcription in S phase cells. Having said that, I am not sure if this small S phase transcription is noise (low cell counts?) or a real S phase specific regulation of transcription which is not DNA content dependent. This results is one of the most central ones in this paper to differentiate between transcriptional and translational scaling. Therefore, additional data or insights would be highly appreciated.

It is possible that the discontinuity in the medians of the S phase population in Figure 4C could be the result of noise due to the low cell count in the short size bins (115 cells at 6.5 µm, 404 at 7.5 µm). In addition, because we cannot measure DNA with a degree of accuracy high enough to identify how advanced in S-phase each cell is, we do not know the distribution of the advancement into S-phase of cells for each length bin. This is complicated by the fact that some cells of the CCP∆ mutant start S-phase whilst still septated and might be in a late S-phase stage by the time the cell splits so the median global transcription of the shorter length bin does not necessary reflect the median of early S-phase cells. Hence the discontinuity observed with cell length does not necessarily suggest that there is a discontinuity happening through S-phase. We suggest that since the mean global transcription per cell length of cells in S-phase is in between the mean global transcription per cell length of cells in G1 and in G2, the increase happens through S-phase. To reflect this possibility we have added “It is also possible that the increase happens at a certain stage of S-phase independent of the amount of DNA since we do not know the extent of S-phase of each cell.”

Minor comments: Line 61: "patterns of protein RNA". I guess this refers to patterns of protein/RNA synthesis?

“patterns of protein and RNA” has been changed to “patterns of protein and RNA synthesis”.

Line 248: typo "Tanslation"

“Tanslation” has been changed to “Translation”.

Line 410 and 416: Move interquartile ranges from line 416 to line 410 as this is the first occurrence of the IQR abbreviation.

“Interquartile ranges” has been moved from line 416 to line 410.

Line 473: "Almost linear". This is a subjective expression, please provide some measure such as the R2 value to quantitatively evaluate linearity in this strain.

We have added a measure of the deviation from linearity in the text “, 15 % deviation from the OLS linear regression shown in Figure 1F”. Line 547: Is there a reason to stress in this experiment that the AREA of the fluorescence signal was measured as the area indicates the total fluorescence intensity?

“area of the” has been replaced by “total” so the sentence refers to the total fluorescence intensity signal of Sytox Green. Fig1A: The schematic mentions peptides, shouldn't it be more accurate to use "polypeptides" or "proteins" when discussing protein synthesis?

“Peptides has been changed to Polypeptides”

Fig 5G: Y axis scale has a typo in the word transcription.

“Trancription” has been changed to “Transcription”

CROSS-CONSULTATION COMMENTS I also agree with the points raised by the colleagues. There will always be some technical or interpretation issues related to every experimental technique, every model system and every mutant strain used. I believe after addressing these limitations as pointed out in the reviews, most of those issues have been clarified for the readers.

Reviewer #4 (Significance (Required)):

Basier and Nurse revisit the classic question regarding growth and cell size control by examining scaling of global translation and transcription in fission yeast. Knowing how cells alter their transcription and translation has important consequences in cellular functions during proliferation and cellular aging and is of broad general interest. The main driver for this current work is that previous experiments both in fission yeast and other model organisms have yielded conflicting results, possibly due to different cell cycle synchronization methods. The strength of the paper is indeed in the single cell analyses of well defined yeast strains which allow accurate assessment of the cell cycle dependent changes and accurate measurements of cell size using the cell length.

Reassuringly, the single cell analyses from unperturbed yeast cells resemble those recently obtained from unperturbed growth of individual mammalian cells. The main conclusion that transcription is not limiting translation, and consequently not limiting growth of the cells, is interesting as it is not consistent with some of the prevailing ideas in the cell size field. These ideas include ploidy dependent gene expression where DNA content is thought to be limiting growth or the model for minimal gene expression which assumes RNA polymerases are limiting gene expression and growth. In this regard, this manuscript provides important insights for future thinking of how growth is controlled.

keywords: cell cycle, cell size control

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

Learn more at Review Commons

Referee #4

Evidence, reproducibility and clarity

Summary

Single cell measurements (flow cytometry and imaging) from unperturbed cells are obtained to investigate scaling of transcription and translation in fission yeast. A key finding is that translation and transcription are somewhat differentially responding to changes in cell size and cell cycle. Perhaps the most central finding of this manuscript is that transcription is not a limiting factor to translation and suggests that transcription is not limiting growth (increase in biomass).

Major comments:

What I like in this manuscript is that the translation and transcription measurements have been carefully checked to reflect the initial rates before the HPG and EU signals lose their linearity. More generally, experiments have been conducted with appropriate controls, and the analysis of unperturbed cells in each cell cycle phase is likely to be highly relevant for resolving some of the controversies in the field. Most claims and the conclusions are well supported by the data.

Although it is encouraging that the results for translation match the single cell mass measurements in mammalian cells (e.g., ref 18), I would have liked to see some more discussion about the potential caveats of the performed analyses such as the low signal to noise ratio in EU incorporation and other potential technical issues, which might have confounded the results. As an example, looking at Figs 1B and E, most of the protein and RNA synthesis signal is nuclear localized. Is this due to nucleolar staining and incorporation of the labels into nascent ribosomes? Yet the manuscript mentions that roughly half of RNA is for rRNA and for ribosomal proteins the fraction of HPG incorporation might be even lower. This statement does not sound entirely consistent with the experimental images shown in Fig 1. Please clarify.

A curious thing that has been glossed over is that the transcription and translation seem not to be completely linear but to display opposite patterns (translation slightly reducing, transcription slightly overshooting with cell size compared to a linear model). It remains possible that this could be experimental noise and a visual pattern that is not real, but it could also be relevant for growth control. For example, my interpretation from Fig. 2B is that the signal is not linear and starts to saturate around 10.5 um cell length as seen from the upper IQR. Related to this, I think it is oversimplification to force the data to appear as a discontinuous linear trend by splitting the data in 2H into two segments. Such a treatment will obviously match the data better than a single linear regression, but perhaps some nonlinear model would be actually much more accurate, unless you can point out some kind of regulatory event at the intersection of these two linear segments. In my opinion the current data looks more like a typical (logarithmic) growth curve of the cell population reaching saturation. Please comment.

The main conclusion presented in the abstract is that scaling in transcription may result from dynamic equilibrium between RNA polymerases and available DNA template. This is a bit of speculative part, which I was not too fond of. The dynamic equilibrium idea has been suggested also elsewhere (refs 47) and is not well developed in this manuscript. There is a lack of mechanistic understanding and no formal (mathematical) model to support this idea. For example, global transcription increases much less (1.3-1.4x) than expected based on the increase in DNA content from G1 to G2 (2x). Is this expected based on the dynamic equilibrium model?

I am somewhat concerned about the interpretation of the S phase data in the global transcription measurement. The quantification in Fig. 4D shows S phase being intermediate between G1 and G2. Yet, when you look at the data in Fig. 4C, the S phase median is clearly discontinuous, with higher transcription in smaller S cells. I believe this could affect the normalized data in Fig. 4D and result in the apparent increase in transcription in S phase cells. Having said that, I am not sure if this small S phase transcription is noise (low cell counts?) or a real S phase specific regulation of transcription which is not DNA content dependent. This results is one of the most central ones in this paper to differentiate between transcriptional and translational scaling. Therefore, additional data or insights would be highly appreciated.

Minor comments:

Line 61: "patterns of protein RNA". I guess this refers to patterns of protein/RNA synthesis?

Line 248: typo "Tanslation"

Line 410 and 416: Move interquartile ranges from line 416 to line 410 as this is the first occurrence of the IQR abbreviation.

Line 473: "Almost linear". This is a subjective expression, please provide some measure such as the R2 value to quantitatively evaluate linearity in this strain.

Line 547: Is there a reason to stress in this experiment that the AREA of the fluorescence signal was measured as the area indicates the total fluorescence intensity?

Fig1A: The schematic mentions peptides, shouldn't it be more accurate to use "polypeptides" or "proteins" when discussing protein synthesis?
Fig 5G: Y axis scale has a typo in the word transcription

Referees cross-commenting

I also agree with the points raised by the colleagues. There will always be some technical or interpretation issues related to every experimental technique, every model system and every mutant strain used. I believe after addressing these limitations as pointed out in the reviews, most of those issues have been clarified for the readers.

Significance

Basier and Nurse revisit the classic question regarding growth and cell size control by examining scaling of global translation and transcription in fission yeast. Knowing how cells alter their transcription and translation has important consequences in cellular functions during proliferation and cellular aging and is of broad general interest. The main driver for this current work is that previous experiments both in fission yeast and other model organisms have yielded conflicting results, possibly due to different cell cycle synchronization methods. The strength of the paper is indeed in the single cell analyses of well defined yeast strains which allow accurate assessment of the cell cycle dependent changes and accurate measurements of cell size using the cell length.

Reassuringly, the single cell analyses from unperturbed yeast cells resemble those recently obtained from unperturbed growth of individual mammalian cells. The main conclusion that transcription is not limiting translation, and consequently not limiting growth of the cells, is interesting as it is not consistent with some of the prevailing ideas in the cell size field. These ideas include ploidy dependent gene expression where DNA content is thought to be limiting growth or the model for minimal gene expression which assumes RNA polymerases are limiting gene expression and growth. In this regard, this manuscript provides important insights for future thinking of how growth is controlled.

keywords: cell cycle, cell size control

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

Summary

Basier and Nurse use fission yeast as a model system to investigate how transcription and translation are coupled to cell-cycle progression. They use metabolic labeling in exponentially growing cells and analyze single cells by microscopy. They find that translation scales with size and increases at S/G2 and early mitosis while transcription increases with both size and the amount of DNA. They suggest that changes in CDK activity regulate changes in global translation rates.

Major comments:

1. The paper addresses a much-disputed question in the field. The approach makes the most of the fission-yeast model system and the experiments are beautifully performed. The conclusions are well supported by the data. The experiments are replicated adequately and the statistical analyses are appropriate.
2. The use of cdc25 and in particular the cig1Δ cig2Δ puc1Δ mutants to manipulate cell size is not without challenges when monitoring translation rates. A number of reports in different model organisms suggest that CDK activity can regulate translation. Work from the Nurse lab identified translation factors as CDK substrates (Swaffer et al, 2016), RNApolIII activity and thus tRNA levels are regulated in the cell cycle by CDK in budding yeast (Herrera et al, 2018), phosphorylation of the ribosomal protein RPL12 by CDK1 is required for translation of at least some proteins in mitosis in human cells (Imami et al, 2018), as is phosphorylation of DENR (Clemm von Hohenberg et al, 2022). The authors also suggest that changes in CDK activity might be responsible for the observed changes in global translation rates. It is important to consider whether using mutants impinging on CDK activity might lead to under- or overestimating cell-cycle dependent translation. The authors should either discuss this issue and tune down the hypothesis that CDK activity regulates changes in global translation rates, or use another approach to address the issue. One could use a replication mutant such as cdc17 or cdc20 to alter cell size without interfering with CDK activity. These experiments would strengthen the conclusions and might support the idea that CDK activity regulates changes in global translation rates.

References

Clemm von Hohenberg K, Müller S, Schleich S, Meister M, Bohlen J, Hofmann TG, Teleman AA (2022) Cyclin B/CDK1 and Cyclin A/CDK2 phosphorylate DENR to promote mitotic protein translation and faithful cell division. Nat Commun 13: 668

Herrera MC, Chymkowitch P, Robertson JM, Eriksson J, Bøe SO, Alseth I, Enserink JM (2018) Cdk1 gates cell cycle-dependent tRNA synthesis by regulating RNA polymerase III activity. Nucleic Acids Res 46: 11698-11711

Imami K, Milek M, Bogdanow B, Yasuda T, Kastelic N, Zauber H, Ishihama Y, Landthaler M, Selbach M (2018) Phosphorylation of the Ribosomal Protein RPL12/uL11 Affects Translation during Mitosis. Mol Cell 72: 84-98 e89

Swaffer MP, Jones AW, Flynn HR, Snijders AP, Nurse P (2016) CDK Substrate Phosphorylation and Ordering the Cell Cycle. Cell 167: 1750-1761 e1716

Minor comments:

1. The figures are beautifully presented, easy to understand and the cartoons present the experimental strategies very clearly.
2. A major feature of the approach is that translation and transcription are monitored in exponentially growing cells, which are not exposed to any stress such as cell-cycle synchronization. However, one could argue that the analogues used for labeling impose some kind of stress, even if this is not very likely at the labeling times employed. A simple control experiment where the growth rates of labeled and unlabeled cells are compared would strengthen the claim that these are indeed happily growing cells.
3. Please comment why the length of the EU labeling differs from figure to figure. In fig 2C, S2C and S2D the labeling on the y axes states 10 min, in Fig 4C it says 20 min.
4. Lines 118-119 "The pulse signal was five times the background signal." Figure S2A,B show large variation in signal intensity after 5 min labelling. It is not clear how the pulse signal was estimated to be five times the background signal.
5. In Fig S4C transcription is up by ca 60 % from G1 to G2, while in Fig 4D transcription is up by ca 25-30%, also from G1 to G2. The only difference I can see is the use of PCNA-GFP. Please comment what the reason might be.
6. Fig 1 B images of unlabeled control cells should also be shown.
7. Lines 156 "to investigate how global cellular translation and transcription are affected by cell size, and by progression through the cell cycle" should be amended. Throughout the description of data in figure 2 binucleated and septated cells were excluded from the analyses, meaning that the data only represent cells in G2. The text should make this clear.
8. Lines 241-243 "the S-phase subpopulation was found to have an intermediary global transcription value between the G1 and G2/M subpopulations of around 20-25 %." And Lines 310-313 "the rate of transcription is increased in cells undergoing S-phase by 20 % and is 35 % higher in G2 cells which have completed S-phase, indicating that DNA content is limiting the global rate of transcription." It is unclear what the percentage values refer to and which populations exactly are being compared.
9. Line 85 "Asynchronous cultures ... have not detected" rephrase; change detected to displayed or similar.
10. Line 243 Figure 4J, K should read Figure 4C, D.

Referees cross-commenting

I also agree with the comments made by the colleagues. As for the use of the cyclin and cdc25 mutants: I agree with Reviewer #1 that it is unlikely that bulk synthesis rates are conisedarably different, since these strains are going at more or lass normal rates. However, I also agree with reviewer #2 that these mutants cannot be considered as unperturbed conditions. I suspect subtle regulation and in particular cell-cycle dependent regulation might well be lost. At the very least the focus of the interpretation should be on translation/transcription as a function of size, rather than in terms of cell-cycle regulation.

Significance

Basier and Nurse address a long-standing question in the cell-cycle field, namely how/whether transcription and translation are coupled to cell-cycle progression. This is technically challenging to address, and many previous studies were hampered by the necessity to synchronize the cells in the cell cycle. The approach of this study of using metabolic labeling in non-synchronized cells is not novel in itself. However, the analysis by microscopy is superior to previous flow-cytometry based strategies in that it allows the use of cell-cycle markers and thereby precise identification of cells in each cell-cycle phase. In addition, it allows accurate measurements of cell size and thus addressing questions of correlations between cell size and transcription / translation rates. A further strength of the study design is that they investigate both transcription and translation in parallel.

The authors very nicely review the existing literature and point out the likely reasons for conflicting conclusions (synchronization methods, choice of model system). The advantages of their approach, such as single-cell analyses in non-synchronized cells and the use of cell-cycle markers make their conclusions less likely to be flawed and thus represent an important advance in the field.

These findings are of interest for researchers working on the cell-cycle field and on the translation field. There have been significant technical advances in the translation field in recent years, allowing studying not only global translation but also translation of specific mRNAs. I expect that the old questions of coupling cell cycle and cell growth will be revisited also by others, exploiting these new approaches. My field of expertise extends to the cell-cycle field and the regulation of translation and the use of fission yeast.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary: Basier and Nurse investigate how "cell size, the amount of DNA, and cell cycle events affect the global cellular production of proteins and RNA molecules". Both transcription and translation, driving the production of biomass, have been shown to increase as a function of cell size in various systems. However, whilst cell size generally correlates with cell cycle progression there are inconsistent results in the literature if global cellular translation and transcription is affected by cell cycle state. They argue that this might be due to perturbations induced by different synchronisation methods used in the various studies.

Therefore, in this study, to avoid potential perturbation from synchronisation methods, they developed a system that allows to assay unperturbed exponentially growing populations of fission yeast cells. The assay is based on single-(fixed)cell measurements of cell size, cell cycle stage, and the levels of global cellular translation and transcription. This allows them to correlate cell cycle state, cell size and global cellular translation and transcription levels at the single cell level under unperturbed conditions.

Their results show that translation and transcription steadily increase with cell size, but that the rate of translation, but not transcription, becomes rapidly restricted when cells become larger than wild type dividing cells. This suggests that it is unlikely that the synthesis of RNA is the limiting factor for translation rate in large cells. In addition, their data indicates that translation scales with size, but that the rate increases faster at late S-phase/early G2 and even faster in early in mitosis before decreasing in mitosis and return to interphase. Transcription, on the other hand, increases as a combination of size and the amount of DNA. Overall, this suggests that cell cycle control affects global cellular translation and transcription, which is in line with some studies, but not others. As far as I can tell the assays and data analysis are robust and the data supports the general conclusions.

Major comments

I agree that inconsistent results published on this topic might be due to perturbations induced by different synchronisation methods used in the various studies. However, but much less emphasised in the paper, it also likely depends on the model system used. For example, in budding yeast there is strong evidence for gene expression homeostasis, i.e. gene expression increases as a function of size, independent of gene copy number. Do the authors believe this is a budding yeast specific phenomenon or is this a consequence of specific synchronisation methods used in budding yeast?

Whether growth rate increases linearly or exponentially has been the topic of decade long debates. Their data indicates that the translation rate increases faster at late S-phase/early G2 and even faster early in mitosis before decreasing in mitosis and return to interphase, 'resetting' the growth rate. This suggest an exponential, rather than linear, increase in biomass (i.e. growth rate?), but this is not explicitly pointed out. It would be good to get the authors opinion on this in the discussion.

The authors state that their approach has allowed them to determine how cellular changes are arising from progression through the cell cycle. However, they use fixed cells, rather than live cell imaging, so can't claim to have established changes during cell cycle progression, but only a correlation with cell cycle state/phase. Whilst this could be used as a proxy for progression it should be clearly stated in the abstract and elsewhere to prevent confusion. I for one, based on the abstract, thought they developed a live cell imaging strategy to look at this.

In reference to the Stonyte, et al., study, in addition to different conditions (temperature shift and isoleucine medium), why do the authors think their findings are different? Is it the lack of correlation to cell size in the Stonyte paper or something else? For example, would using different growth conditions (as in the Stonyte paper). where fission yeast cells spend more time in G1, be used instead of the CCP mutant? Can the authors exclude that the lack of G1-S/cyclin-CDKs is not at the basis of a lower rate of translation in G1 and S phase cells? Either these experiments should be carried out or this should be discussed in more detail.

If the signal to noise signal is reduced by 20 minutes EU incubation (rather than 10 minutes) why wasn't it used in all experiments? And the conclusion that the increase in transcription is not showing any discontinuities, are they referring to the triplicates in the supplementary figure 2?

Minor comments

Lines 168-169: should be Figure 2F, S2C, S2D rather than Figure 2C, S2A, S2B.

Line 179: doubling time instead of growth rate?

Lines 184-186: There is an overall trend of slight decrease in transcription per length in cdc25-22 cells but a slight increase in wild-type cells. How does this differ to wild-type cells? Are these non-significant changes and could these be attributed to the low signal to noise ratio?

There is no cell size that is specific to S phase, it falls within the range of G1 and G2 cells. Since this strain has a variable onset of S phase, the phase durations could differ. Therefore, could time spent in each phase affect the translation rate (live cell imaging, i.e. progression, could address this, but not fix cell correlation)?

The data reflects translation/transcription in single cells at a specific cell cycle phase, not during the transition between cell cycle phases. Therefore, it would be more appropriate to only use G1, S, G2 and M rather than S/G2 transition or early G2.

In figure 4C, there is a decrease in global transcription after 13 um (black line showing all cells), which they don't see in cdc25-22 mutants. Their conclusion that global transcription is constantly increasing with cell size is based on cdc-25 cells but the experiment in CCP mutant cells shows a decrease in the median of transcription. Are there replicates for these experiments as in figure 2 and supplementary figure S2? Maybe an average trend can be plotted too? Apart from the first set of experiments (figure 2 and supplementary figure 2), they don't show replicates for other strains. Maybe they can include another graph as in figure 3D and 3K of average replicate values?

Referees cross-commenting

I believe that since the whole premise of this study is that by using unperturbed conditions their findings are different from previously published work they should either clearly point out that this difference might be due to using mutations affecting CDK activity or carry out an experiment in media that induces a G1 population. CDK has been strongly implicated in promoting translation. Using a strain that lacks the G1 and S cyclin CDKs or compromised M-CDK is therefore likely to have an effect on translation, which could be at the basis of the increase in translation during the G2 (and S) phase of the cell cycle.

Significance

As far as I can tell the assays and data analysis are robust and the data supports the general conclusions. However, whilst the cells are assessed in unperturbed conditions, they do use CDK mutants and the cdc25ts mutant to establsih gene expression during the different phases of the cell cycle, which could affect translation/transcription rates. This should either be clearly pointed out or complemented with an experiment where WT cells are grown in conditions that induces distinct G1-S-G2 populations of cells.

Overall, the work presented suggests that cell cycle control affects global cellular translation and transcription, which is in line with some studies, but not others. Whilst the study falls short of testing/establishing the (potential) mechanisms involved, these are important findings, which can be used to guide new studies into how the production of biomass is controlled as cells proceed through the cell cycle.

The cell size field, which is considerable and growing, will be interested in this work.

I have expertise in cell cycle control and genome stability, with a focus on the G1-to-S transition and cell cycle checkpoints during interphase.

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Referee #1

Evidence, reproducibility and clarity

Basier and Nurse revisit the fundamental question of how the rates of RNA and protein synthesis scale with cell size. The strong null hypothesis is that synthesis scales linearly with cell size: cells that are twice as big should make stuff twice as fast. This hypothesis has been tested many times, in many systems, using many approaches over the past century and, in general, the null hypothesis has been sustained. However, there have been many examples of evidence for more complicated synthetic patterns. Whether these results indicate that biosynthesis rates vary across the cell cycle, or in response to other factors, in addition to increasing with cell size, or whether observed deviations from the predictions of the null hypothesis has been due to artifacts of cell synchronization and labeling, is thus an open, interesting and, because biosynthesis rates have critical implications in cellular function and metabolic robustness, important question.

The authors address the question in fission yeast using metabolic pulse labeling with a ribonucleoside or amino acid analog in asynchronous cells and single cell analysis to directly compare incorporation levels with cell size and cell cycle stage. The experiments are well designed, well executed and well controlled. Furthermore, the data is well presented and appropriately interpreted. In particular, the presentation of the size-v.-label data in Figures 2A and D, with the averages and variances in 2B and E and the normalized data in 2C and F are easy understand and interpret. It is thus notable that the size-v.-label data for the longer (cdc22-22) cells is omitted in favor of just the average (2H,J) and normalized (2I,K) data. This size-v.-label data should be added to Figure 2. The authors should also explicitly state how they chose 15 µm as the inflection point in 2H; 16-17 µm seems like it would give a horizontal plateau, which would better fit their saturation explanation.

The authors measure DNA content with a DNA-binding dye, the signal from which should linearly scale with DNA content. However, instead of reporting and analyzing total signal from the DNA-binding dye (or better yet, total signal in the nucleus, which they could do, having segmented the nucleus in their images), they report max signal. Using max signal is complicated because, as cells and thus nuclei increase in size the concentration of DNA and thus the max (but not total) DNA-binding-dye signal in in the nucleus decreases, requiring two-dimensional dye/size analysis (such as shown in Figure 3B) to distinguish G1 and G2 cells. The authors should use the more straight forward measure of total nuclear DNA-binding dye signal, or explicitly explain why they can't or prefer not to do so.

The authors should state in figure legends the strain numbers used for all experiments. They should also cite the source of all the constituent parts (e.g. hENT1, hsvTK, EGFP-pcn1, and synCut3-mCherry) of their strains.

Referees cross-commenting

My colleagues make constructive points. I agree with all of them, although I am less concerned about the use of cdc2-22 and CCP∆ to alter cell length and cell cycle distribution. Although these mutations alter CDK specific activity (and thus length and distribution) and could alter specific patterns of translation, the fact that they double at normal rates makes it seem unlikely that they could be significantly changing bulk synthesis rates.

Significance

As noted above, this work addresses an open, interesting and important question. Moreover it provides useful data in a specific system and a useful example of a general experimental approach to the problem. However, it does not settle the question of how biosynthesis scales with size, even in the specific case of fission yeast. In particular, it shows that protein synthesis plateaus just above normal cell size, whereas RNA synthesis scales up to twice normal cell size. This observation is striking, because there is no obvious mechanism that would (and the authors offer no suggestion of how to) explain how protein synthesis could be limited if RNA synthesis is not. Therefore, the strength of the paper is that it identifies an intriguing phenomena and its limitation is that it does not provide any testable hypotheses to explain that phenomena.

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Reply to the reviewers

1. General Statements

We thank the reviewers for their critical analysis of our manuscript. We have addressed all reviewer concerns and questions in our revised version. Along with other improvements requested by the reviewers, we added an MTT assay to validate our flow cytometry assays, normalized binding to surface area to better compare toxin binding between Leishmania and HeLa cells, and revised the discussion. We believe the revised contribution provides important novel insights into membrane integrity in a non-standard organism that will appeal to a broad audience.

Reviewer comments below are in italics.

Point-by-point description of the revisions

Reviewer 1

*Major Comments. The experimental work has been carried out carefully, including multiple biological replicates, convincing statistical analysis. Data presentation is extensive, including 6 supplementary figures. It is likely that the experiments could be reproduced by others, as the approaches do not seem to be especially difficult, and the methods are well documented. *

We thank the reviewer for this assessment.

*My major comment regarding revision is that this paper is quite long and extensive given the relatively restricted body of experiments and discrete conclusions. The principal discovery is that sphingolipids protect Leishmania parasites against somewhat artificial treatment with bacterial sterol-binding pore forming toxins, but they do not do so by obstructing toxin binding to sterols. A similar effect is seen for the antileishmanial drug amphotericin B, the most important agent studied. No further mechanistic insights are provided regarding the process whereby sphingolipids blunt toxicity of either the CDCs or amphotericin B. In addition, the experimental approach relies largely upon one methodology, dose-response curves. A report with such highly focused scope should be presentable with considerably more economy. In particular, the Discussion is long and diffuse, obscuring the presentation of the major conclusions. It could probably be cut in half and would in the process present the major deliverables of the paper with higher impact. *

We have condensed the discussion as requested, and to address Reviewer 2’s concerns, we provided a summary articulating the significance.

Significance

*The most notable advance is the observation that sphingolipids protect Leishmania parasites from the cytotoxic activity of the first line antileishmanial drug amphotericin B that binds to the major sterol in the parasite plasma membrane, ergosterol, and induces pore formation. This discovery suggests that parallel treatments with agents that selectively reduce sphingolipid levels in the parasite might act synergistically with amphotericin B, potentially allowing treatment with lower doses of this inherently toxic drug. This work will likely be of most interest to those with a focus on pharmacology and drug development for this and related parasites, but it will also be of some interest to those working on the basic biochemistry of these organisms. The senior authors are major workers in sphingolipid biochemistry in Leishmania parasites and thus are well positioned to address the relevant background in the field, much of which has come out of their laboratories.

The major limitation of this study is its relatively circumscribed scope, resulting in one principal conclusion: Leishmania sphingolipids blunt the potency of toxins or drugs that target sterols for pore formation, but they do not do so by impairing binding of these agents to sterols, as they do in mammalian cells. The work would be of higher impact if it addressed mechanistically how sphingolipids do decrease toxicity, e.g., do they prevent these agents from oligomerizing or from intercalating into the membrane to form pores. Such studies would require the application of an expanded repertoire of experimental methodologies going beyond the measurement of dose-response curves with various mutants and drugs.*

We agree with the reviewer that next steps include determining if Leishmania sphingolipids interfere with oligomerization or pore-insertion. One challenge is that these tools need to first be validated in Leishmania.

To address the reviewer concern about the limited range of experimental methodologies, we added an MTT assay (Supplementary Fig S2E) as validation of our flow cytometry assays. We have better summarized the significance and broad impact of our work in lines 466-476.

Reviewer 2

*In the abstract the authors describe that the pore-forming toxins engage with ceramide and other lipids and while it's clear that the levels of sphingolipids are important for the effect of these toxins there is limited evidence to show they physically interact as the word engage suggests. *

We agree with the reviewer that we do not show physical interaction. In the abstract, we are careful to only use the word “engage” in association with our proposed model. Our proposed model both explains our data, and uses those data to open new horizons by making falsifiable predictions that can be tested in the future. Direct engagement of toxins with lipids is one such prediction. For these reasons, we prefer to retain the word “engage” in the abstract.

*The authors conclude that the ergosterol on the Leishmania cell membrane is less accessible to the CDCs as it does not bind as much CDCs as a HeLa cell. What is the relative abundance of sterols in the HeLa membrane in comparison to a Leishmania cell. A HeLa cell is much bigger than a Leishmania cell and will therefore be able to bind a lot more CDC, was the MFI normalised for cell size? This would be important to know as the difference in intensity may be purely related to the difference in cell size. *

We thank the reviewer for this insight. We had not normalized MFI by cell surface area. We added MFI normalized to cell size (described on lines 573-577) and found that when area was accounted for, the promastigotes bound more toxin than HeLa cells. These data are now included as Supplementary Fig S1A, and discussed on lines 187-189.

*The authors are keen to prosecute that ceramide is important for differences between PFO and SLO action as the inhibitor has a much greater effect on the PFO treatment of ipcs- cells than SLO, as ceramide will accumulate in these cells. But for the SLO analysis they stated that the treatment of spt2- with myriocin had no change on the LC50 as the target of myriocin was spt2 while they noted was there a drop in the LC50 with PFO. Based on this I think the importance of ceramide is being overstated here, as spt2- cells have little ceramide in them. Moreover the authors also suggest that changes to the lipid environment rather than a single species might be important. Are there alternative targets the myriocin might inhibit when there is no spt2-, it is intriguing that there is a decrease in LC50 for PFO on spt2- myriocin treated cells. *

Clearly, IPC is very important for determining the cytotoxicity for the CDCs in Leishmania but I think the evidence for the role of ceramide and the sensing of it is less clear cut and the strength of the conclusions about this should be modified. In the results the authors conclude that the L3 loop is sensing ceramide and the data shows that the L3 loop is important but in the discussion they are more circumspect about the moieties L3 can detect. The authors should qualify these conclusions in the results a bit more.

As requested by the reviewer, we have qualified our statements in the results, lines 282, 297, 315.

*Minor comments *

*It would be helpful for the review process to include line and page numbers to highlight areas that I have concerns about. *

We agree with the reviewer and have added line numbers.

*In the first paragraph of the results is there a reference for the spt2- cell line that was used here. *

We have added the Zhang 2003 reference to the first paragraph of the results, line 161.

*In the second paragraph there is a disconnect between the statements about the phenotype of the ipcs- cells and the reference/evidence for it. *

We have added the reference to the earlier mention of the ipcs cells, and in the introduction, lines 118-120 and 167-169.

*On many of the graphs the letters a, b, c are alongside many of the symbols but it was unclear what they represented. *

The letters represent statistically distinct groups. These are used instead of stars and bars to reduce clutter on the figure. We have now explained the difference in the first figure legend in which they are used, lines 818-823.

*The colour scheme for figure 4 was confusing - yellow diamonds in A/B are spt2-/+spt2 but in C/D are iscl-, this makes it hard to compare between them. *

We have changed the color and symbols for the iscl- mutant in Fig 4 and Fig S6.

*The methodology states that various tests were used to define whether differences were significant but it was not clear from the figures when these were being applied only a few graphs had '*' associated with them. *

We have clarified this in the figure legends.

*There is no overall conclusion to the study at the end of the discussion just a series of limitations of the study, which is good to acknowledge but feels an odd way to finish the manuscript. *

We have revised the discussion in response to Reviewer 1, and included a summary to tie everything together, lines 466-476.

*Significance: *

Overall this is a strong manuscript with a set of experiments that have a clear strategy and purpose that was well written. This paper outlines the importance of the lipid composition for the cytotoxicity of both sterol specific toxins and amphotericin B in Leishmania, which will have significant implications for their study for other pathogens but also for the development of combination therapies to enhance the potency of amphotericin B, as such I think this will be of interest to both researchers interested in drug discovery and those interested in lipid metabolism.

We thank the reviewer for this assessment.

Reviewer 3

Major comments: 1) The idea that sphingolipids do not block toxin access relies on the work of CDC-based probes binding the accessible pool of cholesterol in mammalian membranes. The authors make the observation that ergosterol is not shielded by sphingolipids because the presence of them does not prevent CDC binding. Is it possible to show that Leishmania sphingolipids are able to actually sequester ergosterol or would it all be considered free and available to toxin binding?

Our interpretation of the binding data is that the Leishmania sphingolipids fail to sequester ergosterol from toxins, so ergosterol accessibility is independent of sphingolipids. Similar to mammalian cells, there could be an “essential” pool of ergosterol bound to other proteins/lipids that is inaccessible to toxins. However, detecting that pool is technically challenging.

We have revised the manuscript to clarify this, lines 454-456.

* 2) The statistical analysis applied to each experiment, while defined in the figure legends, are presented mostly using uncommon methods of presentation, making it difficult to determine if the correct analysis was applied.*

We have clarified the statistics and use of letters. The letters represent statistically distinct groups. These are used instead of stars and bars to reduce clutter on the figure. We have now explained the difference in the first figure legend in which they are used, lines 818-823.

* 3) The binding of these toxins to Leishmania cells appears to be independent of their lipid composition, but Figure 1A-D suggests that these toxins do not bind very well to Leishmania; a ~65 fold increase in toxin added only results in a maximal 3 fold change in amount of toxin bound. Therefore, the authors need to demonstrate that this increase in binding is not simply the result of adding more ug of each CDC. *

Leishmania are smaller than HeLa cells, which accounts for the apparent reduced binding. We added Supplementary Fig S1A, which normalized MFI to estimated surface area. When normalized to surface area, Leishmania bound to toxin better than HeLa cells. We further note that the dose-dependent increase in cytotoxicity argues against non-specificity of increased toxin.

* 4) The authors use HeLa cells to compare the ability of these toxins to bind to sterol containing membranes, but it is unclear how a mammalian cell line, which lacks ergosterol, can inform upon the differences in binding to Leishmania membranes when their data shows almost no cholesterol is found in the Leishmania membrane. The use of HeLa cells to compare the toxicity of these CDCs is simply a control experiment for the lytic activity of these proteins, and should not be used as a direct comparison of their LC50s, as a mammalian plasma membrane lipid composition is significantly different from that of Leishmania. If the authors want to use HeLa cells as a direct comparison to show that sphingolipids in mammalian cells also protect them from CDC pore formation, they must demonstrate the HeLa cells which have genetic defects in sphingolipid biology or which have been treated with sphingomyelinases are more sensitive to these CDCs. *

We agree with the reviewer that to argue sphingolipids in mammalian cells are protective would require additional data beyond the scope of this manuscript. We are not making any statements about the role of sphingolipids in mammalian cells, which have a controversial role in CDC damage and membrane repair (see e.g. Schoenauer et al 2019. PMID: 29979630). Since the head group of sphingomyelin interacts with cholesterol (Endapally et al 2019), but the IPC head group is not expected to interact similarly with ergosterol, we choose to remain focused on Leishmania sphingolipids.

Given our focus on Leishmania, why include HeLa cells at all? We think including HeLa cells provides an important and relevant point of reference because there are situations where both human cells and Leishmania promastigotes could encounter pore-forming toxins. This comparison provides insight to the following question: “In a mix of promastigotes and human cells (for example during a blood meal), which cells would die first from the bacterial PFT?” Comparing cytotoxicity to HeLa cells provides a point of reference in judging how cytotoxic CDCs are to Leishmania promastigotes, and how sensitive the spt- promastigotes become.

We have rephrased the manuscript (lines 208-209) to better clarify that HeLa cells are a reference point so readers can evaluate the relative sensitivity of sphingolipid-deficient promastigotes.

* 5) The authors need to demonstrate that the mutant cholesterol recognition motif (CRM) and the glycan binding mutant proteins can still bind to both Leishmania and Hela cell membranes to serve as controls for their lack of lytic activities. Without this, they cannot conclude that "Leishmania membranes engage the same binding determinants used by CDCs to target mammalian cells". *

The glycan binding and ΔCRM mutants are unable to bind to HeLa cells. These toxin mutations were previously characterized (Mozola & Caparon, 2015 and Farrand et al 2010), showing that their defect lies in binding to cells, but not oligomerization or pore-formation. Since their defect lies solely in binding, if these toxins were able to bind to spt2- cells, they would kill the spt2- cells. This enables us to use these toxin mutants to ask if the CRM or glycan-binding is essential for toxin binding to Leishmania. Since the only defect in these mutant toxins is binding (either to glycans or cholesterol), the failure of these mutants to kill allows us to conclude that both of these binding surfaces on the toxin are essential for cytotoxicity in L. major.

We have clarified the manuscript, lines 236-240. *

Minor comments: 6) Multiple figures lack adequately defined axes. Examples include, but are not limited to: Figure 1A-D where the X-axis is plotted as logarithmic based 2 but this is not defined. Figure 2 the Y axis is plotted as logarithmic based 10 but is not defined. *

We have updated the figure legends to indicate where log axes are used.

7) The authors state that "Promastigotes with inactivated de novo sphingomyelin synthesis has a significant increase in total sterols" in reference to Figure 1E. Not only is there no significance indicated for the spt2-/-, the authors only indicate a significance point for the Myr (not yet defined) + WT sample in "Other sterols".

We have rephrased this to indicate a trend, line 181.

8) The authors use increases in membrane permeability as a read out for specific lysis using PI uptake, however, they then refer to this read out as killing of Leishmania, without measuring the viability of these cells. Therefore, the authors should provide additional experiments that demonstrate the death of the different Leishmania strains treated with the cytolysins.

As requested, we have now provided an additional experiment to validate Leishmania death. We have now added MTT assay as Fig S2E, and discussed in the results, lines 202-205.

9) It is not clear how the authors calculated their LC50 values in Figure 2. According to the figure legends, the authors used HU/ml ranges that would be sub lethal or not completely lysed within this range to most of the Leishmania strains tested. The data presented in Figure are not clear that the correct LC50 calculations were used as none of the Specific Lysis curves do not reach saturation with the concentrations presented, and one does not even reach 50% Lysis.

We thank the reviewer for catching this discrepancy. The legend in Fig 2 did not include the correct ranges of toxin dose used for PFO. We have corrected the legend to indicate the toxin range used. To calculate LC50, we used linear regression on the linear portion of the death curve to determine the concentration at 50% lysis. This gives us a way to determine LC50 even without the use of very large (and costly) amounts of toxin to get extensive saturation on the kill curve.

* 10) Figure 4 and Figure S6 are very difficult to interpret. Figure S6 would benefit by breaking up each graph into multiple graphs that would allow the reader to see more of the curves individually. Additionally, there are multiple conditions were it appears that a different number of experiments (2-4 totals) were preformed but statistical analysis was applied to these data. *

We updated the labels on Fig 4 for improved readability. We broke Fig S6 up into multiple graphs. We have removed unpaired data (eg the n of 4 noted by the reviewer), and re-checked our stats. This change did not alter our conclusions. The apparent n of 2 was overlap of data points due to poor jittering of the datapoints. We have increased the jitter on the data points to make all three reps more distinct.

* 11) The authors state "In contrast to myriocin-treated ipcs- L. major, which contain low levels of ceramide, myriocin treated iscl- L. major contain low levels of IPC" but do not provide a reference or point to data to support this claim. *

We have qualified these statements to say ‘are expected to’ on lines 306-307.

* 12) Figure 5 E would benefit in presentation by being broken up into 4 separate graphs based on the toxin used, as it is difficult to determine which data points are being compared. *

We compare by toxin used in Fig 5A-D. The purpose of Fig 5E is to compare between toxins. We included all of the data points (including resistant control strains) for completeness. The main focus is the spt2- and ipcs- parts of Fig 5E.

* 13) The authors state that "myriocin did not inhibit growth more than 25% promastigotes at 10 μM" but this data is not presented. *

We have now added these data as Fig 6A.

14) Multiple graphs lack legends or have axis that are not defined.

In order to improve readability and avoid cluttering the figures, where the legends and axes are the same across multiple graphs, they are included only once for a given row and/or column.*

Significance:

Overall, the experiments presented were conducted to analyze each question, but many of the results are observational, without considering the impact of altered lipid species on the findings. The data suggests an existence of a protective mechanism for the parasite from CDCs, but it unclear how these finding inform upon the CDC or Leishmania fields. CDCs have been known to target sterols within membranes and that altered local membrane environments can have substantial impacts on CDC binding. This work suggests that the altered lipid species of Leishmania membranes, compared to a mammalian membrane, could dramatically effect the sequestering power of sphingolipids or other lipids, and thus change how CDCs bind to them. This work advances is likely to have specialized audience of Leishmania researchers looking at the dynamics of their membranes.*

We believe this work will be valuable to a broad audience because it will be of interest to researchers studying membranes in general, pathogenic eukaryotes and pore-forming toxins. Most membrane biology work is done either in opisthokonts or in model liposomes, so there are few studies on biomembranes in other taxonomic groups, including many different human pathogens. We provide a blueprint for examining the membranes of non-standard organisms, establish L. major as a pathogenically relevant model system, and report on key differences in sterol sequestration compared to mammalian cells. These findings provide important perspectives for the generalization of biomembranes, especially when compared to prior work in opisthokonts.

We have clarified our significance in lines 466-476.

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Referee #3

Evidence, reproducibility and clarity

Haram & Moitra et al. report a mechanism by which the lipid environment of the Leishmania membrane determines the effects of two different pore forming toxins. They demonstrate that sphingolipids protect Leishmania from toxin-induced cytotoxicity without effecting the proteins ability to bind to the membrane. They further demonstrate that ceramide can reduce the cytotoxicity of the toxins through the sensing of the local lipids, and that this composition can protect Leishmania from first line antibiotics. The manuscript follows a model for explaining this protection, but several important questions and controls remain and need to be addressed.

Major comments:

1. The idea that sphingolipids do not block toxin access relies on the work of CDC-based probes binding the accessible pool of cholesterol in mammalian membranes. The authors make the observation that ergosterol is not shielded by sphingolipids because the presence of them does not prevent CDC binding. Is it possible to show that Leishmania sphingolipids are able to actually sequester ergosterol or would it all be considered free and available to toxin binding?
2. The statistical analysis applied to each experiment, while defined in the figure legends, are presented mostly using uncommon methods of presentation, making it difficult to determine if the correct analysis was applied.
3. The binding of these toxins to Leishmania cells appears to be independent of their lipid composition, but Figure 1A-D suggests that these toxins do not bind very well to Leishmania; a ~65 fold increase in toxin added only results in a maximal 3 fold change in amount of toxin bound. Therefore, the authors need to demonstrate that this increase in binding is not simply the result of adding more ug of each CDC.
4. The authors use HeLa cells to compare the ability of these toxins to bind to sterol containing membranes, but it is unclear how a mammalian cell line, which lacks ergosterol, can inform upon the differences in binding to Leishmania membranes when their data shows almost no cholesterol is found in the Leishmania membrane. The use of HeLa cells to compare the toxicity of these CDCs is simply a control experiment for the lytic activity of these proteins, and should not be used as a direct comparison of their LC50s, as a mammalian plasma membrane lipid composition is significantly different from that of Leishmania. If the authors want to use HeLa cells as a direct comparison to show that sphingolipids in mammalian cells also protect them from CDC pore formation, they must demonstrate the HeLa cells which have genetic defects in sphingolipid biology or which have been treated with sphingomyelinases are more sensitive to these CDCs.
5. The authors need to demonstrate that the mutant cholesterol recognition motif (CRM) and the glycan binding mutant proteins can still bind to both Leishmania and Hela cell membranes to serve as controls for their lack of lytic activities. Without this, they cannot conclude that "Leishmania membranes engage the same binding determinants used by CDCs to target mammalian cells".

Minor comments:

1. Multiple figures lack adequately defined axes. Examples include, but are not limited to: Figure 1A-D where the X-axis is plotted as logarithmic based 2 but this is not defined. Figure 2 the Y axis is plotted as logarithmic based 10 but is not defined.
2. The authors state that "Promastigotes with inactivated de novo sphingomyelin synthesis has a significant increase in total sterols" in reference to Figure 1E. Not only is there no significance indicated for the spt2-/-, the authors only indicate a significance point for the Myr (not yet defined) + WT sample in "Other sterols".
3. The authors use increases in membrane permeability as a read out for specific lysis using PI uptake, however, they then refer to this read out as killing of Leishmania, without measuring the viability of these cells. Therefore, the authors should provide additional experiments that demonstrate the death of the different Leishmania strains treated with the cytolysins.
4. It is not clear how the authors calculated their LC50 values in Figure 2. According to the figure legends, the authors used HU/ml ranges that would be sub lethal or not completely lysed within this range to most of the Leishmania strains tested. The data presented in Figure are not clear that the correct LC50 calculations were used as none of the Specific Lysis curves do not reach saturation with the concentrations presented, and one does not even reach 50% Lysis.
5. Figure 4 and Figure S6 are very difficult to interpret. Figure S6 would benefit by breaking up each graph into multiple graphs that would allow the reader to see more of the curves individually. Additionally, there are multiple conditions were it appears that a different number of experiments (2-4 totals) were preformed but statistical analysis was applied to these data.
6. The authors state "In contrast to myriocin-treated ipcs- L. major, which contain low levels of ceramide, myriocin treated iscl- L. major contain low levels of IPC" but do not provide a reference or point to data to support this claim.
7. Figure 5 E would benefit in presentation by being broken up into 4 separate graphs based on the toxin used, as it is difficult to determine which data points are being compared.
8. The authors state that "myriocin did not inhibit growth more than 25% promastigotes at 10 μM" but this data is not presented.
9. Multiple graphs lack legends or have axis that are not defined.

Significance

Overall, the experiments presented were conducted to analyze each question, but many of the results are observational, without considering the impact of altered lipid species on the findings. The data suggests an existence of a protective mechanism for the parasite from CDCs, but it unclear how these finding inform upon the CDC or Leishmania fields. CDCs have been known to target sterols within membranes and that altered local membrane environments can have substantial impacts on CDC binding.

This work suggests that the altered lipid species of Leishmania membranes, compared to a mammalian membrane, could dramatically effect the sequestering power of sphingolipids or other lipids, and thus change how CDCs bind to them.

This work advances is likely to have specialized audience of Leishmania researchers looking at the dynamics of their membranes.

Expertise: I study host-pathogen interactions with a focus on plasma membrane lipids and cholesterol.

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Referee #2

Evidence, reproducibility and clarity

Summary

One of the major treatments of the parasitic disease Leishmaniasis is the drug amphotericin B, which targets ergosterol and a route to increasing its potency would be to increase the accessibility ergosterol on the surface of the parasite. With that in mind the authors investigated sterol-binding ability of two cytotoxic toxins PFO and SLO. The authors clearly show that these toxins are readily able to bind to the surface of the parasite regardless of the levels of sphingolipids present, yet the presence of inositol phosphorylceramide and to a lesser extent ceramide affect overall cytotoxicity. The L3 loop of the toxin was shown to be important for the sensitivity of the different toxins to the lipid composition of the membrane.

Major comments

In the abstract the authors describe that the pore-forming toxins engage with ceramide and other lipids and while it's clear that the levels of sphingolipids are important for the effect of these toxins there is limited evidence to show they physically interact as the word engage suggests.

The authors conclude that the ergosterol on the Leishmania cell membrane is less accessible to the CDCs as it does not bind as much CDCs as a HeLa cell. What is the relative abundance of sterols in the HeLa membrane in comparison to a Leishmania cell. A HeLa cell is much bigger than a Leishmania cell and will therefore be able to bind a lot more CDC, was the MFI normalised for cell size? This would be important to know as the difference in intensity may be purely related to the difference in cell size.

The authors are keen to prosecute that ceramide is important for differences between PFO and SLO action as the inhibitor has a much greater effect on the PFO treatment of ipcs- cells than SLO, as ceramide will accumulate in these cells. But for the SLO analysis they stated that the treatment of spt2- with myriocin had no change on the LC50 as the target of myriocin was spt2 while they noted was there a drop in the LC50 with PFO. Based on this I think the importance of ceramide is being overstated here, as spt2- cells have little ceramide in them. Moreover the authors also suggest that changes to the lipid environment rather than a single species might be important. Are there alternative targets the myriocin might inhibit when there is no spt2-, it is intriguing that there is a decrease in LC50 for PFO on spt2- myriocin treated cells.

Clearly, IPC is very important for determining the cytotoxicity for the CDCs in Leishmania but I think the evidence for the role of ceramide and the sensing of it is less clear cut and the strength of the conclusions about this should be modified. In the results the authors conclude that the L3 loop is sensing ceramide and the data shows that the L3 loop is important but in the discussion they are more circumspect about the moieties L3 can detect. The authors should qualify these conclusions in the results a bit more.

Minor comments

It would be helpful for the review process to include line and page numbers to highlight areas that I have concerns about.

In the first paragraph of the results is there a reference for the spt2- cell line that was used here.

In the second paragraph there is a disconnect between the statements about the phenotype of the ipcs- cells and the reference/evidence for it.

On many of the graphs the letters a, b, c are alongside many of the symbols but it was unclear what they represented.

The colour scheme for figure 4 was confusing - yellow diamonds in A/B are spt2-/+spt2 but in C/D are iscl-, this makes it hard to compare between them.

The methodology states that various tests were used to define whether differences were significant but it was not clear from the figures when these were being applied only a few graphs had '*' associated with them.

There is no overall conclusion to the study at the end of the discussion just a series of limitations of the study, which is good to acknowledge but feels an odd way to finish the manuscript.

Significance

Overall this is a strong manuscript with a set of experiments that have a clear strategy and purpose that was well written. This paper outlines the importance of the lipid composition for the cytotoxicity of both sterol specific toxins and amphotericin B in Leishmania, which will have significant implications for their study for other pathogens but also for the development of combination therapies to enhance the potency of amphotericin B, as such I think this will be of interest to both researchers interested in drug discovery and those interested in lipid metabolism.

Expertise in the molecular cell biology of trypanosomes and leishmania.

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Referee #1

Evidence, reproducibility and clarity

Summary.

In this manuscript the authors demonstrate that sphingolipids protect Leishmania major promastigotes from the toxic effects of two bacterial cholesterol-binding cytolysins (CDCs), polypeptide toxins that first bind to sterols in cellular membranes and then oligomerize to form pores. More significantly for Leishmania biology, sphingolipids also protect the parasites against similar pore forming activity by the first line antileishmanial drug amphotericin B, suggesting that treatments that reduced the levels of sphingolipids, especially ceramide and inositol-phosphoceramide (IPC), might enhance selective potency of amphotericin for the parasite and thus allow lower doses of this inherently toxic drug to be applied. The experimental work is based largely on dose-response curves of wild type, spt2- mutants (fail to make sphingolipids), ipcs- mutants (do not synthesize IPC and build up the precursor ceramide), and the respective add-back lines with and without treatment with myriocin that inhibits the SPR enzyme and thus blocks sphingolipid biosynthesis. These bacterial toxins, although not directly relevant to Leishmania biology, are used as a model to investigate sensitivity to sterol-binding pore forming agents, and sensitivity to the antileishmanial drug amphotericin B, which parallels the bacterial toxins in binding to ergosterol and forming membrane pores, is also found to be enhanced when sphingolipid levels are reduced. Notably, sphingolipids do not reduce the binding of CDCs to ergosterol in the parasite membrane, as they do in mammalian cells, but rather act downstream of sterol binding, possibly by reducing pore forming activity by some unknown mechanism.

Major Comments.

The experimental work has been carried out carefully, including multiple biological replicates, convincing statistical analysis. Data presentation is extensive, including 6 supplementary figures. It is likely that the experiments could be reproduced by others, as the approaches do not seem to be especially difficult, and the methods are well documented.

My major comment regarding revision is that this paper is quite long and extensive given the relatively restricted body of experiments and discrete conclusions. The principal discovery is that sphingolipids protect Leishmania parasites against somewhat artificial treatment with bacterial sterol-binding pore forming toxins, but they do not do so by obstructing toxin binding to sterols. A similar effect is seen for the antileishmanial drug amphotericin B, the most important agent studied. No further mechanistic insights are provided regarding the process whereby sphingolipids blunt toxicity of either the CDCs or amphotericin B. In addition, the experimental approach relies largely upon one methodology, dose-response curves. A report with such highly focused scope should be presentable with considerably more economy. In particular, the Discussion is long and diffuse, obscuring the presentation of the major conclusions. It could probably be cut in half and would in the process present the major deliverables of the paper with higher impact.

Minor Comments:

Except for my comment about the length of the manuscript (which I consider to be a major comment for this paper), I have no further suggestions on this topic.

Significance

The most notable advance is the observation that sphingolipids protect Leishmania parasites from the cytotoxic activity of the first line antileishmanial drug amphotericin B that binds to the major sterol in the parasite plasma membrane, ergosterol, and induces pore formation. This discovery suggests that parallel treatments with agents that selectively reduce sphingolipid levels in the parasite might act synergistically with amphotericin B, potentially allowing treatment with lower doses of this inherently toxic drug. This work will likely be of most interest to those with a focus on pharmacology and drug development for this and related parasites, but it will also be of some interest to those working on the basic biochemistry of these organisms. The senior authors are major workers in sphingolipid biochemistry in Leishmania parasites and thus are well positioned to address the relevant background in the field, much of which has come out of their laboratories.

The major limitation of this study is its relatively circumscribed scope, resulting in one principal conclusion: Leishmania sphingolipids blunt the potency of toxins or drugs that target sterols for pore formation, but they do not do so by impairing binding of these agents to sterols, as they do in mammalian cells. The work would be of higher impact if it addressed mechanistically how sphingolipids do decrease toxicity, e.g., do they prevent these agents from oligomerizing or from intercalating into the membrane to form pores. Such studies would require the application of an expanded repertoire of experimental methodologies going beyond the measurement of dose-response curves with various mutants and drugs.

Reviewer's areas of expertise: Biochemistry, cell, and molecular biology of parasitic protozoa.

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Reply to the reviewers

Comments received from the Reviewers on 18th of November 2022 are included in plain font, followed point-by-point by the authors’ comments in bold.

Reviewer #1 (Evidence, reproducibility and clarity):

The endothelial release of NRG (neuregulin)-1 is a paracrine growth factor activating ErbB (erythroblastic leukaemia viral oncogene) receptor tyrosine kinases on various targets cells epicardial, endocardial/endothelial (autocrine stimulation) and myocardiocytes. It is well known, after the manuscript of the K.D.Poss group that Neuregulin1 induced perivascular cells after injury to the adult zebrafish heart as well as mammalian cells. Inhibition of the Erbb2 co-receptor, disrupts cardiomyocyte proliferation in response to injury, whereas myocardial NRG1 overexpression enhances this proliferation. Thus, seems to be clear, that NRG-1 could stimulate regenerative, inflammatory, fibrotic, and metabolic processes In uninjured zebrafish, the reactivation of Nrg1 expression induces cardiomyocyte dedifferentiation, overt muscle hyperplasia, epicardial activation, increased vascularization, and causes cardiomegaly through persistent addition of wall myocardium (review cited by authors in this MS). In light of the large amount of these research deals with NRG1, the molecular mechanisms linked and focused to understand the multivariate effects of the NRG1 cascade are welcome. The authors have focused the manuscript on a comparative and translational demonstration of STAT5b involvement in the signal transduction of NRG1.

Although the authors have done several experiments they have presented these in a chaotic way among mice, zebrafish and human biopsies. I can suggest rewriting partially the results section in a way more ordered and readable. Even the discussion is a little bit chaotic and lacks some aspects. For example, who is the stimulator of NRG1 release? Moreover, the literature cited is partially or not correctly reported (in the references section). In my opinion, the authors should revise the manuscript in the light of following suggestions.

MAJOR:

Title: line 1. The title does not explain the translational aspects of the manuscript. I suggest something like: "STAT5b is a key effector of NRG1/ERBB4-mediated cardiomyocyte growth: a translational approach".

We have now modified the title as suggested by the Reviewer.

Abstract. Lines 20-25. The authors should rewrite this section by removing their previous finding ("we") reporting. In lines 25-36 the reported data is not well explained and is not clear who did that. The authors, previously? It is not well explained.

Lines 35-37 Please, specify in which type of hypertrophic heart samples (is it from humans?) have been observed the NRG1 pathway.

We have now rewritten this section of the abstract and changed the tense to present to better indicate which observations are presented in the manuscript.

Introduction. Lines 44-46. All the cited papers consist of the preprint, thus they could be inserted in the discussion and not in the introduction. In the alternative, they could be inserted here following a sentence "Preliminary study seems to indicate...."

We apologize for the mistake, the references are not preprints but articles published in Nature. We have amended the reference section so this is now indicated more clearly.

Lines 50-51. The references cited are relative only to murine research and not to other animals. Thus, only murine models have been demonstrated. Thus, the assertion could be not valid for zebrafish or humans, thus the authors should point out this.

The reference number 8 in the original submission refers to experiments conducted in embryonic zebrafish. We have now rewritten this section by separating the previous observations in mice and in zebrafish into separate sentences.

Material and Methods.

Lines 148-150. The authors should explain in which way they have treated the embryos. For example, have they treated the embryos in an immersion way of what?

We have now added the requested information in the Materials and Methods section.

Lines 159-160. Vanadates serve as structural mimics of phosphates. Thus it acts as a competitive inhibitor of ATPases, alkaline and acid phosphatases, and protein-phosphotyrosine phosphatases. The authors should explain the reason for the use of this chemical as a control.

This chemical was not used as a control, but included in both the NRG-1 and control injections. This is now more clearly indicated in the Materials and Methods section. Pervanadate was added to the injections to ensure that pSTAT5 signal is not lost during sample preparation during which the larvae were kept in room temperature for 20 minutes after injection. The peak for pSTAT5 signal according to our previous research after NRG-1 stimulation is already at around 1-2 minutes and after 15 minutes the signal is already fading. We did attempt the experiment without the pervanadate and the results indeed were similar although the difference between the control and NRG-1 injections was less pronounced.

Lines 179-181. The fish cells are partially autofluorescent. The authors did not use any system to remove the autofluorescence or, perhaps they lack to indicate in the text (i-e- pre-exposure under UV or Sudan black treatment).

While the authors agree on the potential contribution of autofluorescence on the background signal, this was not considered a significant confounding factor in the experimental conditions described in the manuscript. Indeed, the myosin heavy chain antibody gave a clear bright signal and the STAT5 stainings were validated with the loss of signal in the Stat5b targeting CRISPR/Cas9 treated zebrafish.

Results. This section should be rewritten in order by differentiating the data from zebrafish, murine and humans. For example, I can guess that the title on line 330 is referred to zebrafish, but it is not indicated in the title and the text.

We have now more clearly separated the results from mice and zebrafish.

Discussion. This section should be revised in light of the previous suggestion because not bring the reader to have a clear idea of the importance of this research. Thus, I suggest preparing a clear discussion on 1) who or what can stimulate the NRG1 release by endothelial cells (or also from other activated cells, i.e. endocardial); 2) if this release is similar in vertebrates studied models; 3) If the pathway studied is similar and when it is different. All these points should be documented by references. Moreover, the authors could correlate the manuscript with a draw that explains the signalling pathway that they suggest.

We have now added the suggested information on NRG-1 release in the Introduction and added a new paragraph to the Discussion where we compare the reported differences of the NRG-1/ERBB4 pathway in mice and in zebrafish. In addition, we have included a new figure (Figure 7) that explains the signaling pathway, as recommended by the Reviewer.

References:

The molecular pathways that direct the process of reactivation of proliferation processes and hypertrophy are beginning to be elucidated with evidence that fibroblast growth factors, and microRNAs involvement that can be the starting time before NRG1 expression. Thus, in Mammals as well as fish the authors should read and mention some of the linked previous research (J Physiol 596.23 (2018) pp 5625-5640; Nat Med. 2007 May;13(5):613-8. doi: 10.1038/nm1582; Cardiovasc Res (2015) 107, 487-498 doi:10.1093/CVR/cvv190; Cell Death Discovery 4, 41 (2018) https://doi.org/10.1038/s41420-018-0041-x)

We have added a new paragraph to the discussion section where we discuss the interplay of the NRG-1 signaling pathway with other pathways reported to induce cardiomyocyte growth.

MINOR:

References 4 and 5 are pre-print, please indicate the correct final reference

We again apologize for the mistake. The references are now amended to refer to the correct articles published in Nature.

Reference 14 resulted in an invalid URL address. The manuscript resulted non-existent

We apologize for the mistake. The URL had accidentally doubled in the reference. We have now amended the URL.

Reference 19 is incomplete

Reference 20 not exhaustive is a personal communication, thus should be removed from here and reported in the text as "personal communication"

Reference 27 is incomplete

Reference 42 is incomplete

Reference 69 is incomplete

We apologize for the mistakes. We have amended the shortcomings in the reference section.

Reviewer #1 (Significance):

The Manuscript could be interesting for the readers, but need a deeper revision in the presentation and mainly in the Result-Discussion section.

The Results and Discussion sections have now been revised as recommended by the Reviewer.

After the revision, the manuscript will be of marked interest to cardiologists.

The authors agree and wish to thank the Reviewer for valuable comments.

Reviewer #2 (Evidence, reproducibility and clarity):

RC-2022-01698 Review

The authors report that NRG-1/ERBB4 signaling regulates activation of STAT5b and its target genes Igf1, Myc and Cdkn1a in murine cardiomyocytes, both in vitro and in vivo. STAT5b is a key activator in mediating NRG-1-induced cardiac hypertrophy in rodents. The NRG-1-ERRB4-STAT5 signaling axis is conserved in vertebrates since it regulates cardiomyocyte hyperplasia in zebrafish and is active in human hearts with pathological hypertrophy. Mechanistically, dynamin-2 was shown to control the cell surface localization of ERBB4 and its inhibition downregulates the NRG-1-ERRB4-STAT5 signaling pathway in hypertrophic and hyperplastic cardiomyocyte growth.

The study is reasonably well conducted, experiments are controlled and quantified and most conclusions drawn by the authors are supported by their own data.

This work is of high significance since it uncovers a mechanism responsible for cardiomyocyte hypertrophy which is perturbed in pathological cardiac hypertrophy. This finding opens the possibility that targeting STAT5 activation in patients with cardiomyopathy and heart failure might ameliorate the disease. It is of special note that NRG-1-ERRB4-STAT5 signaling promotes cardiomyocyte proliferation in zebrafish, a species known for its high cardiac repair capacity. This suggests the intriguing possibility that Stat5 could play an important role also in heart regeneration.

A major shortcoming is the presentation of the scientific questions and what this paper is abou could be improved.

As noted also above, the Introduction, Results and Discussion sections have now been revised as recommended by the Reviewers.

Major comments:

1. The use of the NRG1 scavenger should be validated. The provided reference #28 does not validate it. In the reference ____#28, it is reported that ERBB4 phosphorylation is downregulated with the scavenger in mice treated with AAV-VEGFB. The effect of the expression of the NRG-1 scavenger is detectable by western analysis in the mice treated with the AAV-VEGFB (Figure 6A,E) since the treatment induces prolonged activation of ERBB4 by upregulating the release and synthesis of ERBB4 ligands. Additionally, in a control pull-down experiment, the NRG-1 scavenger did bind NRG-1 from mouse serum (please see Rebuttal Figure 1).

It is conceivable that direct manipulation of STAT5 might have effects independent from NRG-1/ERBB4 signaling and therefore might affect also hyperplasia in addition to hypertrophy. This study would benefit from additional experiments showing the proliferation rate (quantified with e.g. H3P or Aurora B) upon Stat5 knockdown or ERBB inhibition in murine cardiomyocytes.

The proliferation rate of adult cardiomyocytes in uninjured models has been reported to be very low, less than 1% (Bergmann et al., 2009. Science. 324:98-102). For this reason we employed an immortalized dividing murine adult cardiomyocyte cell line, HL-1 Claycomb et al., 1998. Proc Natl Acad Sci U S A. 17:95:2979-84.), to address the question raised by the Reviewer. HL-1 cells were transduced with control and Stat5b-targeting shRNAs and cultured on 24-wells in the presence of NRG-1. The amount of HL-1 cells treated with Stat5b-targeting shRNAs was significantly smaller as compared to cells treated with control shRNA 72 hours after transduction (Rebuttal Figure 2A). However, it seems that increased cell death significantly contributed to the observed decrease in cell number as an increase of dead cells was observed in wells treated with Stat5b shRNAs when the cells were stained with a cell permeable (blue) and cell-impermeable (green) nuclear stain (Rebuttal Figure 2B-C). In accordance, the expression of the proliferation marker PCNA was unaltered by the Stat5b shRNA treatment in western analyses (Rebuttal Figure 2D). Thus, it seems that STAT5b does not control the proliferation rate but the viability of dividing adult mouse cardiomyocytes. The observation is not surprising since STAT5b has been reported to control the expression of the anti-apoptotic BCL2 and BCL-xL in adult cardiomyocytes (Chen et al. 2018. Cardiovasc. Res. 114:679-689).

In lines 504-507, the authors write: "In accordance, the target genes of STAT5b IGF1 and MYC have been associated with hypertrophic and hyperplastic growth, respectively, implying that the STAT5b mediated hypertrophic growth may be mediated by the expression of MYC and the hyperplastic growth by the expression of IGF1". The authors cannot make this conclusion because both MYC and IGF1 are downregulated in murine cardiomyocytes. If hyperplastic growth is not regulated by NRG-1-ERRB4-STAT5 signaling in mice, then IGF1 expression should be unaffected by any manipulation of the pathway. It is suggested that the authors modify this statement to accurately reflect their data.

We have decided to remove this conjecture from the discussion as suggested by the Reviewer.

In lines 564-566, the authors write: "In accordance with clinical applicability, administration of NRG-1 and the protein product of the STAT5b target gene IGF1 has demonstrated success in attenuating dilated cardiomyopathy in clinical trials". STAT5 is already activated in pathological cardiac hypertrophy as shown in Figure 6C-D. How can the authors explain how administration of the STAT5 target gene IGF1, thus potentiating the effect of STAT5 activation, could reduce hypertrophy and thus ameliorate the disease?

Left-ventricular hypertrophy is considered a compensatory response to increased pressure-overload and only if left unattended can lead to dilated cardiomyopathy. There is growing evidence that NRG-1/ERBB4 signaling is lost when the compensatory hypertrophic growth advances to dilated cardiomyopathy (Rohrbach et al., 2005. Basic Res. Cardiol. 100:240-9; Rohrbach et al., 1999. Circulation. 100:407-12.) which may suggest that the loss of the NRG-1/ERBB4 signaling is one of the factors that contributes to the progression of the disease. Therefore it would be feasible that the reactivation of the signaling pathway that was active during the compensatory response could ameliorate the disease. As we also indicate that the NRG-1/ERBB4/STAT5 pathway is involved in the proliferative growth of cardiomyocytes at embryonic stage in zebrafish, an organism known for its high cardiac regenerative capability (Poss et al., 2002. Science. 298:2188-90.), it is also feasible that the NRG-1/ERBB4/STAT5 pathway is involved in cardiac regeneration. Lastly, there is growing evidence that NRG-1, IGF-1 and STAT5b are also involved in cardiomyocyte survival (Mehrhof et al., 2001. Circulation. 104:2088-94; De Keulenaer et al., 2019. Circ. Heart Fail. 12:e006288; Chen et al., 2018. Cardiovasc. Res. 114:679-689) and therefore could alleviate the symptoms of dilated cardiomyopathy by compelling the cardiomyocytes more resistant to cell death. There are reports that suggest that cardiomyocyte apoptosis is increased and putatively even has a causal role in dilated cardiomyopathy (Yamamoto et al., 2003. J. Clin. Invest. 111:1463-74; Wencker et al., 2003. J. Clin. Invest. 111:1497-504.).

Minor comments:

1. Increase in cardiomyocyte numbers is better evidence for NRG-1-induced hyperplasia in zebrafish compared to increase in ventricle area. It is recommended that the authors swap Figure 3A-B with Supplementary Figure 3 in order to show more clearly the different role of NRG-1 in zebrafish compared to rodents. We have now moved original Supplementary Figure 3 into new Figure 3A as recommended by the Reviewer.

The authors should report the p-value for all experiments including those considered not statistically significant.

The non-significant P-values have now been added to the figures.

Reviewer #2 (Significance):

General significance of the reserach ms is high.

The authors wish to thank the Reviewer for valuable comments.

However, the ms is written and the study is conducted with little direction. Perhaps the authors could spend more effort on clearly explaining what the direction of their paper is.

We have now reconstructed the manuscript and paid extra attention into explaining the direction and aim of the research.

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Referee #2

Evidence, reproducibility and clarity

The authors report that NRG-1/ERBB4 signaling regulates activation of STAT5b and its target genes Igf1, Myc and Cdkn1a in murine cardiomyocytes, both in vitro and in vivo. STAT5b is a key activator in mediating NRG-1-induced cardiac hypertrophy in rodents. The NRG-1-ERRB4-STAT5 signaling axis is conserved in vertebrates since it regulates cardiomyocyte hyperplasia in zebrafish and is active in human hearts with pathological hypertrophy. Mechanistically, dynamin-2 was shown to control the cell surface localization of ERBB4 and its inhibition downregulates the NRG-1-ERRB4-STAT5 signaling pathway in hypertrophic and hyperplastic cardiomyocyte growth.

The study is reasonably well conducted, experiments are controlled and quantified and most conclusions drawn by the authors are supported by their own data.

This work is of high significance since it uncovers a mechanism responsible for cardiomyocyte hypertrophy which is perturbed in pathological cardiac hypertrophy. This finding opens the possibility that targeting STAT5 activation in patients with cardiomyopathy and heart failure might ameliorate the disease. It is of special note that NRG-1-ERRB4-STAT5 signaling promotes cardiomyocyte proliferation in zebrafish, a species known for its high cardiac repair capacity. This suggests the intriguing possibility that Stat5 could play an important role also in heart regeneration.

A major shortcoming is the presentation of the scientific questions and what this paper is abou could be improved. Major comments:

1. The use of the NRG1 scavenger should be validated. The provided reference #28 does not validate it.
2. It is conceivable that direct manipulation of STAT5 might have effects independent from NRG-1/ERBB4 signaling and therefore might affect also hyperplasia in addition to hypertrophy. This study would benefit from additional experiments showing the proliferation rate (quantified with e.g. H3P or Aurora B) upon Stat5 knockdown or ERBB inhibition in murine cardiomyocytes.
3. In lines 504-507, the authors write: "In accordance, the target genes of STAT5b IGF1 and MYC have been associated with hypertrophic and hyperplastic growth, respectively, implying that the STAT5b mediated hypertrophic growth may be mediated by the expression of MYC and the hyperplastic growth by the expression of IGF1". The authors cannot make this conclusion because both MYC and IGF1 are downregulated in murine cardiomyocytes. If hyperplastic growth is not regulated by NRG-1-ERRB4-STAT5 signaling in mice, then IGF1 expression should be unaffected by any manipulation of the pathway. It is suggested that the authors modify this statement to accurately reflect their data.
4. In lines 564-566, the authors write: "In accordance with clinical applicability, administration of NRG-1 and the protein product of the STAT5b target gene IGF1 has demonstrated success in attenuating dilated cardiomyopathy in clinical trials". STAT5 is already activated in pathological cardiac hypertrophy as shown in Figure 6C-D. How can the authors explain how administration of the STAT5 target gene IGF1, thus potentiating the effect of STAT5 activation, could reduce hypertrophy and thus ameliorate the disease?

Minor comments:

1. Increase in cardiomyocyte numbers is better evidence for NRG-1-induced hyperplasia in zebrafish compared to increase in ventricle area. It is recommended that the authors swap Figure 3A-B with Supplementary Figure 3 in order to show more clearly the different role of NRG-1 in zebrafish compared to rodents.
2. The authors should report the p-value for all experiments including those considered not statistically significant.

Significance

General significance of the reserach ms is high. However, the ms is written and the study is conducted with little direction. Perhaps the authors could spend more effort on clearly explaining what the direction of their paper is.

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 endothelial release of NRG (neuregulin)-1 is a paracrine growth factor activating ErbB (erythroblastic leukaemia viral oncogene) receptor tyrosine kinases on various targets cells epicardial, endocardial/endothelial (autocrine stimulation) and myocardiocytes. It is well known, after the manuscript of the K.D.Poss group that Neuregulin1 induced perivascular cells after injury to the adult zebrafish heart as well as mammalian cells. Inhibition of the Erbb2 co-receptor, disrupts cardiomyocyte proliferation in response to injury, whereas myocardial NRG1 overexpression enhances this proliferation. Thus, seems to be clear, that NRG-1 could stimulate regenerative, inflammatory, fibrotic, and metabolic processes In uninjured zebrafish, the reactivation of Nrg1 expression induces cardiomyocyte dedifferentiation, overt muscle hyperplasia, epicardial activation, increased vascularization, and causes cardiomegaly through persistent addition of wall myocardium (review cited by authors in this MS).

In light of the large amount of these research deals with NRG1, the molecular mechanisms linked and focused to understand the multivariate effects of the NRG1 cascade are welcome. The authors have focused the manuscript on a comparative and translational demonstration of STAT5b involvement in the signal transduction of NRG1.

Although the authors have done several experiments they have presented these in a chaotic way among mice, zebrafish and human biopsies. I can suggest rewriting partially the results section in a way more ordered and readable. Even the discussion is a little bit chaotic and lacks some aspects. For example, who is the stimulator of NRG1 release? Moreover, the literature cited is partially or not correctly reported (in the references section). In my opinion, the authors should revise the manuscript in the light of following suggestions. MAJOR: Title: line 1. The title does not explain the translational aspects of the manuscript. I suggest something like: "STAT5b is a key effector of NRG1/ERBB4-mediated cardiomyocyte growth: a translational approach".

Abstract.

Lines 20-25. The authors should rewrite this section by removing their previous finding ("we") reporting. In lines 25-36 the reported data is not well explained and is not clear who did that. The authors, previously? It is not well explained. Lines 35-37 Please, specify in which type of hypertrophic heart samples (is it from humans?) have been observed the NRG1 pathway.

Introduction.

Lines 44-46. All the cited papers consist of the preprint, thus they could be inserted in the discussion and not in the introduction. In the alternative, they could be inserted here following a sentence "Preliminary study seems to indicate...." Lines 50-51. The references cited are relative only to murine research and not to other animals. Thus, only murine models have been demonstrated. Thus, the assertion could be not valid for zebrafish or humans, thus the authors should point out this.

Material and Methods.

Lines 148-150. The authors should explain in which way they have treated the embryos. For example, have they treated the embryos in an immersion way of what? Lines 159-160. Vanadates serve as structural mimics of phosphates. Thus it acts as a competitive inhibitor of ATPases, alkaline and acid phosphatases, and protein-phosphotyrosine phosphatases. The authors should explain the reason for the use of this chemical as a control. Lines 179-181. The fish cells are partially autofluorescent. The authors did not use any system to remove the autofluorescence or, perhaps they lack to indicate in the text (i-e- pre-exposure under UV or Sudan black treatment).

Results. This section should be rewritten in order by differentiating the data from zebrafish, murine and humans. For example, I can guess that the title on line 330 is referred to zebrafish, but it is not indicated in the title and the text.

Discussion. This section should be revised in light of the previous suggestion because not bring the reader to have a clear idea of the importance of this research. Thus, I suggest preparing a clear discussion on 1) who or what can stimulate the NRG1 release by endothelial cells (or also from other activated cells, i.e. endocardial); 2) if this release is similar in vertebrates studied models; 3) If the pathway studied is similar and when it is different. All these points should be documented by references. Moreover, the authors could correlate the manuscript with a draw that explains the signalling pathway that they suggest.

References:

The molecular pathways that direct the process of reactivation of proliferation processes and hypertrophy are beginning to be elucidated with evidence that fibroblast growth factors, and microRNAs involvement that can be the starting time before NRG1 expression. Thus, in Mammals as well as fish the authors should read and mention some of the linked previous research (J Physiol 596.23 (2018) pp 5625-5640; Nat Med. 2007 May;13(5):613-8. doi: 10.1038/nm1582; Cardiovasc Res (2015) 107, 487-498 doi:10.1093/CVR/cvv190; Cell Death Discovery 4, 41 (2018) https://doi.org/10.1038/s41420-018-0041-x)

Minor

References 4 and 5 are pre-print, please indicate the correct final reference

Reference 14 resulted in an invalid URL address. The manuscript resulted non-existent

Reference 19 is incomplete

Reference 20 not exhaustive is a personal communication, thus should be removed from here and reported in the text as "personal communication"

Reference 27 is incomplete

Reference 42 is incomplete

Reference 69 is incomplete

Significance

The Manuscript could be interesting for the readers, but need a deeper revision in the presentation and mainly in the Result-Discussion section.

After the revision, the manuscript will be of marked interest to cardiologists.

Transparent Peer Review

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

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Referee #2

Evidence, reproducibility and clarity

Summary:

Modulation of protein phosphorylation level is a critical mechanism in the regulation of different cellular processes, whose dysregulation is associated with disease, including cancers. Protein phosphatase (PP)2A is a central phosphatase involved in multiple cellular pathways, including cell cycle, metabolism, and regulation of gene expression. In addition, inactivation of PP2A is required for RAS-mediated human cell transformation, making reactivation of PP2A as a potential therapeutic approach. Aakula, Sharma et al investigated whether RAS and PP2A could co-regulate cellular processes involved in tumorigenesis via the modulation of protein phosphorylation. The authors re-analysed their previously published phosphoproteomics datasets performed after knockdown with siRNAs of RAS (H/K/N), PP2A-A, or PP2A inhibitory proteins (CIP2A, PME1, SET). The authors found a set of phosphosites commonly regulated by RAS and PP2A, which is enriched for proteins involved in the epigenetic regulation of gene expression, including DNA methylation, chromatin remodelling, and chromatin modifications. The authors then investigated how modulating RAS and PP2A activities (by siRNA or small molecule inhibitors) affect the chromatin recruitment of the HDAC1 and HDAC2 proteins, which are part of the NuRD chromatin-remodelling complex. Modulation of RAS and PP2A activities also affects transcription, both with a single GFP gene construct and by RNA-seq, with knockdown of RAS mostly decreasing gene expression while knockdown of PP2A generally associated with increased gene expression. The authors then investigated the genome-wide effects of knocking PP2A on DNA methylation and chromatin accessibility (ATAC-seq) and found a limited number of sites affected.

Major comments:

1. The investigation and characterization of the phosphosites that are common to both RAS and PP2A is an important question, as stated by the authors. However, the authors hardly investigated the potential roles of these common phosphosites (only CHD3 S713 has been partially investigated) but rather relied on knockdown by siRNAs of the factors, which limits the conclusions of the manuscript as it remains unknown whether these phosphosites have any effect on protein activity and/or interactions.
2. The major technical limitation of the manuscript is the dependence on siRNAs to investigate RAS and PP2A. Knockdown by siRNAs takes a long time, which limits the conclusions that can be drawn as the results are going to be a mixture of direct (loss of RAS/PP2A) and indirect (cellular responses to the direct effects) effects. Typically, changes in gene expression, DNA methylation, and chromatin accessibility could be explained, at least in part, by indirect effects of the knockdown (changes in cell cycle, cellular responses to stress induced by the knockdown...). I think it will be important to confirm on some target genes that the main results of the manuscript are direct effects by using known small molecule inhibitors with short treatment time.
3. The genome-wide data do not seem to have been submitted to the GEO (or I could not find the information), which also means that it is not clear how many biological replicates have been performed.
4. Generally, the authors should put more information in the Legends/Methods as several key information are missing (see Minor Comments).
5. The authors should integrate more their RNA-seq, RRBS, and ATC-seq data as these datasets have been generated in the same cell line (I suppose RRBS is also in HeLa, see Minor Comment 2). Do the authors see consistent changes on RRBS/ATAC-seq for the upregulated/downregulated genes?

Minor comments:

1. Did the authors performed a total (with rRNA depletion) or a poly(A)+ RNA-seq?
2. In the Methods section for the RRBS, it is written that the DNA was isolated from the same samples. Is it the same samples as the RNA-seq? More precision is required.
3. It would also be useful to put in the legends the cell line used in each experiment.
4. Figure 3, Figure 4, and Figure S5: I could not find any information on the treatment time and the concentrations of the small molecule inhibitors used. These information need to be added to the legends.
5. Figure 3B: the authors need to performed qRT-PCR to show that the overexpression is similar between the different conditions. Right now, the differences could be explained by a difference in transcription between the different constructs.
6. Also, do the mutations affect CHD3 chromatin association or interaction with other NuRD components? This kind of straightforward experiments would clearly improve the interest of the manuscript as it will provide information on the potential roles of phosphosites.
7. Figure 3C, E, G, and I: A nuclear loading control is required for each experiment. Also, western blots on whole cell extracts are required to see if the changes in nuclear/chromatin level are not just explained by a change in the total expression of HDAC1 and HDAC2 following siRNA treatment.
8. Lines 552-555: I am not convinced that the presence of DOT1L among the regulators associated with open promoter regions provides a direct link between the phosphoproteome and ATAC-seq data. DOT1L is a methyltransferase associated with transcription initiation and transcription elongation and therefore it is not surprising to find this protein in open promoter regions. In addition, to claim a direct link would require data showing that protein phosphorylation of DOT1L regulates its recruitment to promoter regions.
9. Figure 7F/G: Are the overlaps significantly enriched?

Referees cross-commenting

If the manuscript is clearly presented as a ressource paper, I agree with reviewer 1. My major comments 1 and 2 (knockdown of total proteins rather than looking at phosphoresidues, RNAi) can be addressed in the discussion rather than experimentally.

Significance

The mechanistic roles of phosphosites remain generally an understudied area of research while kinases and phosphatases are known to be frequently dysregulated in disease. The generation of a list of phosphosites common to RAS proteins and PP2A is therefore of interest as this will provide targets for further investigation. The authors tested some of the targets by using a siRNA approach, which confirmed the involvement of PP2A in the regulation of gene expression, DNA methylation, and chromatin remodelling/accessibility and of RAS in the regulation of gene expression and chromatin accessibility. However, the authors focused on the proteins rather than the phosphosites, which limits the significance of the work as it remains unclear whether the effects the authors are observing are mediated by changes in phosphorylation level (in addition to the potential issues of indirect effects due to the siRNA approach).

Context:

Loss of PP2A phosphatase activity is required for human cell transformation while RAS is a known oncogene (Chen et al, 2004; Rangarajan et al, 2004). The manuscript investigated which proteins were commonly phospho-regulated by RAS and PP2A activities and found an overrepresentation of proteins involved in transcriptional regulation and epigenetics, which confirms and expands previous observations. PP2A, as part of the INTAC complex that is composed of Integrator and PP2A, has been found to regulate nascent transcription (Vervoort et al, 2021; Zheng et al, 2020). In addition, PP2A activity has also been linked to DNA methylation (Hausser et al, 2006; Kundu et al, 2020; Sunahori et al, 2013) and nuclear localization of several histone deacetylases (HDAC) (Tinsley & Allen-Petersen, 2022).

Audience:

The reported findings will be of interest to people working on the RAS/PP2A-associated cancers, and more generally in the fields of regulation of gene expression, chromatin remodelling, and epigenetics.

Field of expertise:

transcription, chromatin, RNA polymerase II, transcriptional kinases and phosphatases.

References

Chen W, Possemato R, Campbell KT, Plattner CA, Pallas DC, Hahn WC (2004) Identification of specific PP2A complexes involved in human cell transformation. Cancer Cell 5: 127-136

Hausser A, Link G, Hoene M, Russo C, Selchow O, Pfizenmaier K (2006) Phospho-specific binding of 14-3-3 proteins to phosphatidylinositol 4-kinase III beta protects from dephosphorylation and stabilizes lipid kinase activity. J Cell Sci 119: 3613-3621

Kundu A, Shelar S, Ghosh AP, Ballestas M, Kirkman R, Nam H, Brinkley GJ, Karki S, Mobley JA, Bae S et al (2020) 14-3-3 proteins protect AMPK-phosphorylated ten-eleven translocation-2 (TET2) from PP2A-mediated dephosphorylation. J Biol Chem 295: 1754-1766

Rangarajan A, Hong SJ, Gifford A, Weinberg RA (2004) Species- and cell type-specific requirements for cellular transformation. Cancer Cell 6: 171-183

Sunahori K, Nagpal K, Hedrich CM, Mizui M, Fitzgerald LM, Tsokos GC (2013) The catalytic subunit of protein phosphatase 2A (PP2Ac) promotes DNA hypomethylation by suppressing the phosphorylated mitogen-activated protein kinase/extracellular signal-regulated kinase (ERK) kinase (MEK)/phosphorylated ERK/DNMT1 protein pathway in T-cells from controls and systemic lupus erythematosus patients. J Biol Chem 288: 21936-21944

Tinsley SL, Allen-Petersen BL (2022) PP2A and cancer epigenetics: a therapeutic opportunity waiting to happen. NAR Cancer 4: zcac002

Vervoort SJ, Welsh SA, Devlin JR, Barbieri E, Knight DA, Offley S, Bjelosevic S, Costacurta M, Todorovski I, Kearney CJ et al (2021) The PP2A-Integrator-CDK9 axis fine-tunes transcription and can be targeted therapeutically in cancer. Cell 184: 3143-3162 e3132

Zheng H, Qi Y, Hu S, Cao X, Xu C, Yin Z, Chen X, Li Y, Liu W, Li J et al (2020) Identification of Integrator-PP2A complex (INTAC), an RNA polymerase II phosphatase. Science 370

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Referee #1

Evidence, reproducibility and clarity

In this resource manuscript by Aakula et al., the authors reanalyze existing phosphoproteomic datasets to find areas of convergence of proteins and sites regulated by RAS activation on the one hand, and PP2A inhibition on the other. They identify a number of such sites. The validation is relatively modest, showing effects on HDAC1/2 localization, the silencing of an artificial promoter, and then focus on epigenetic regulation in more general experiments. They provide plentiful data and correlations that will be useful for others interested in mechanism of regulation by protein phosphorylation. The major limitation, acknowledged by the authors, is that this is a resource rather than a deep validation of the overlaps.

I have only a few minor specific comments.

The overlap of PP2A and RAS regulated phosphoproteins in the gene ontology networks is made up of small numbers - 3/6 in term 0070087. When only 3 genes are in a category, given the reliability of GO terms, it doesn't generate much excitement.

Likewise the effect of knockdowns of putative targets in NSCLC cells was modest, with 10- 20% decrease in cell viability. I suspect many gene knockdowns might give a similar effect.

Line 299 starts a >1.5 pages long paragraph about CHD3 and HDAC1/2; it would be easier to read if this were two or three shorter paragraphs.

The pulldown data (S5A) is done with over-expressed proteins and shows a weak interaction. Without evidence for endogenous protein interaction, the conclusion that there is a substantial in vivo physiologic interaction between B56α and HDAC1 must be qualified.

Referees cross-commenting

I agree with reviewer 2 that there are shortcomings. If this is viewed as a resource, and not a strong conclusion paper, my feeling is that additional confirmation experiments would not add much. I agree they should be careful to discuss the limitations of the RNAi approach.

Significance

The data suggest that two major cancer mutations converge to influence epigenetic regulators. The data is correlative and will assist future mechanistic studies.

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Reply to the reviewers

[Reviewer's comments]

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

Summary In this article Roure et al address the role of BMP during formation of the ascidian palps, using Ciona intestinalis. Overexpression of BMP (specifically ADMP) from early stages of development results in complete suppression of palp formation, and early loss of the palp forming region (also called anterior neural border ANB). Using p-Smad1/5/8 antibody staining they show a marker of the ANB (FoxC) is expressed in a region negative for BMP signals. Inhibition of BMP signals is not sufficient to produce ectopic ANB. However, treatment with FGF protein from very early stages (8-cell stage) plus inhibition of BMP signaling (from 8-cell stage) increased FoxC expression. Looking at later stages of development the authors show that in a U-shaped expression domain of Foxg, Smad1/5/8 is active in the ventral-most part, which is expected to form the ventral-most palp. BMP2 treatment from gastrula stages results in loss of the ventral most palp expression of Isl and repression of ventral Foxg expression. Inhibition of BMP signaling from gastrula or neurula stages results in failure of a U-shaped pattern of Isl expression to resolve into the three palp expression domains, and by late tailbud stages, Sp6/7/8/9 (proposed as a repressor of Foxg in the inter-palp territory) expression is reduced and the numbers of specific cell-types making up the palps is increased. These cells are present in a single large palp of dorsal identity. Thus, inhibition of BMP from early gastrula stages results in a single palp made of more cells than the three palps of control larvae, presumably due to recruitment of cells usually present between the palps. The authors then show a similar phenotype in another ascidian species Phallusia mammillata. Using their previous RNA-Seq data of embryos treated with BMP4, they looked for potential novel palp markers and identify a further eight novel markers of the palps. Looking further into this data and at a list of 68 genes expressed in palps (but not exclusively) they find that in whole embryo RNA-Seq data 70% were regulated by BMP signaling, mostly repressed, but some activated by BMP. 30 of these genes were regulated by Notch. Apart from the confusion I explained in my comments below, the data seems to be carefully presented and interpreted. Overall, this manuscript presents a more detailed analysis of the role of BMP signaling during ascidian palp formation, but it remains to be precisely understood.

[Response]

We thank the reviewer for the evaluation of our work.

Major comments

1) I am a little confused about the timing of the protein treatments. In Figure 2, the authors show nicely that at the neurula stages, P-Smad1/5/8 staining abuts the FoxC ANB territory. Then at late neurula P-Smad1/5/8 is detected in the ventral-most part of the Foxg U-shaped part of the palp forming region, presumably the ventral most palp. However, the protein treatments with BMP (and FGF) are carried out from the 8-cell stage, which seems a bit drastic and embryos look difficult to orientate (e.g. Fig. 3D).

[Response]

We first would like to clarify the issue raised from Figure 3. Actually, Figure 3D was the only case where the embryo was shown from the side (the description as a lateral view was inadvertently omitted in the legend). We have now modified Figure 3 by properly showing only dorsal (neural plate) views and lateral views in insets when necessary. In addition, we have added schemes of embryos depicting the main tissues we have examined (palps, CNS and epidermis) and their localization depending on the treatments.

Regarding the timing of treatments, we performed them at the 8-cell stage to make them manageable to perform. At the latest, bFGF treatment should be performed at the 16-cell stage (before neural induction at the 32-cell stage), while BMP2 treatment should be performed at the 64-cell stage (before the onset of Foxc/partial effect at early gastrula (St. 10)). In principle, sequential treatment (first bFGF, then BMP2) could thus be performed. Since earlier treatments, produce the same effects, we reasoned that combined treatments from the 8-cell stage should be equivalent and would avoid fastidious repeated manipulation of the embryos that could negatively impact their development. We are convinced that the way we performed the treatment has no impact on our results (except for the treatment by bFGF alone on Foxc as already discussed in the text) and conclusions.

While BMP-treatment from early stages inhibits all palp gene expression and any sign of palp formation (Figure 1), treatment with BMP from the early gastrula stage, when Smad1/5/8 is detected only in mesendoderm cells and before it is detected in any ectoderm, is sufficient only to block ventral palp formation and cause a partial down-regulation of FoxC expression in the ANB. Thus, there seems to be a discrepancy between the roles proposed for BMP during ANB and palp formation as judged by P-Smad1/5/8 staining and the temporal evidence from BMP- and BMP-inhibitor treatment. Do the authors have some explanation for why they need to treat at least one hour before the BMP-mediated patterning mechanism (as indicated from the P-Smad1/5/8 staining) is taking place? For example, could the authors check how long it takes DMH1 to inhibit P-Smad1/5/8 positive staining? Or BMP to strongly induce P-Smad1/5/8? This seems to be a simple experiment and might go some way to explaining why they need to treat embryos much earlier than I would have thought necessary.

[Response]

We understand the reviewer's concerns, but we do not think that there are major discrepancies in the timing of events. The main rationale is to consider the onset of expression for the main genes of interest. We have examined their dynamics of expression in details, but we do not show them since our conclusions are in agreement with a previous report (Figure 1 from Liu and Satou, 2019). We have summarized the data in the modified Figure 2. Foxc can be detected from early gastrula stages (St. 10) when the palp precursors consist of a single row of 4 cells. This is the exact developmental time when the treatment with BMP2 has partial effects (Figure 4). Once the cells divide to make 2 rows of 4 cells robustly expressing Foxc (St. 12), BMP2 treatment has no effect on Foxc. Similarly, DMH1 treatment has no effect from late neurula stage (St. 16) (Figure 4) that corresponds to the onset of Sp6/7/8/9 expression. We thus consider that modulating BMP pathway has no effect once key regulatory genes have acquired a robust expression in their normal domains. We have enhanced these points in the main text (lines 205-208, lines 228-229).

We think the above discussion should address the points raised by the reviewer. In the contrary, we are willing to perform the suggested experiments.

2) It does not make sense to me that BMP treatment from gastrula stage blocks only ventral palp formation (Figure 4) and ventral Foxg expression (Fig. 5G). In particular, it is the ventral palp region which is positive for P-Smad1/5/8 (Fig.2I,J) so I would not expect the ventral palp to be the most sensitive to BMP-treatment.

[Response]

We were, like the reviewer, surprised by the phenotype. The time window to obtain this phenotype is quite narrow, and most likely deals with the full acquisition of the palp fate ('consolidation' of Foxc expression, onset of Foxg). This is actually a phenotype that we have not characterized in details. And such a characterization may help clarify the role of BMP: does BMP regulate papilla/inter-papilla fates only for the ventral palp or for all three palps? Does BMP 'only' regulate the dorso-ventral identities of the palps?

To better understand the role of BMP in palp formation, we propose to describe this specific phenotype: loss of ventral palp induced by BMP2 treatment at St. 10. We propose to test the following hypotheses. What is the fate of the ventral palp? Conversion into epidermis (more ventral fate)? Conversion into inter-papillar fate? What is the identity of the 2 remaining presumptive palps? Do they still have a dorsal identity? Are they converted into ventral palps? This is part of the proposed experiments for a revision.

Minor comments line 185 I see what the authors are trying to say but I don't agree that BMP limits the domain of FoxC expression as inhibition of BMP has no effect on FoxC. Rather BMP has to be kept out of the ANB in order to allow ANB formation.

[Response]

We have modified the sentence (lines 195-196).

The relationship between Foxg and Sp6/7/8/9 expression is not really clear and it would be better to do this with double ISH if the authors want to show mutually exclusive expression domains, or at least provide a summary figure.

[Response]

We have modified Figure 5 by adding schematic representations of our understanding of the expression patterns in relation to the different precursors of the palp lineage.

In case the reviewer does not find this clarification sufficient, we propose to perform the double fluorescent in situ hybridizations as part of the revision plan.

Line 218, I do not see the data showing that Isl is expressed at a U-shape at st. 23, it seems to be expressed in three dots, unless embryos are treated with DMH1.

[Response]

We apologize for the misunderstanding since the sentence was not clear. We referred to the U-shaped Isl expression under BMP inhibition. Indeed, Isl starts to be expressed in 3 separate domains in the palp forming region, and not following a U-shape as its upstream regulator Foxg (Liu and Satou, 2019). We amended the sentence (lines 234-235).

Figure 6B, G. It could be nice to show a close up of the palps to see elongated cells.

[Response]

The close up pictures have now been added in the modified Figure 6.

Figure 6K. It is better to use a statistical test to support the authors conclusions.

[Response]

As suggested, we have performed a statistical evaluation (Mann-Whitney U test) of the cell counts. The p-values are presented in Figure 6Q. The slight increase of Celf3/4/5/6 is not statistically significant, but it does not impact our conclusion that the number of papilla cells increases following BMP inhibition.

It could be nice to provide a timeline for Smad1/5/8 signaling and the role for BMP signals that are proposed in this manuscript as a summary diagram.

[Response]

Following the suggestion, we have added summary diagrams in Figure 2 for BMP signaling in relation to lineages and gene expression.

lines 66-74 is lacking references.

[Response]

This is now corrected (lines 70-80).

Reviewer #1 (Significance (Required)):

Significance While it is still not clear how BMP signals are established (which ligands for example) and their precise role in palp formation, this manuscript adds more information to our current understanding of the role of BMP signaling during palp formation. In particular it shows that BMP signals need to be kept out of the ANB for its formation and that it is required to resolve the later forming palp territory into three discrete palp regions. However, there is some way to go before this is fully understood. This article will certainly be of interest to ascidian developmental biologists trying to understand the formation and patterning of the larval PNS. It may also be of some interest to evolutionary biologists trying to understand the relationship between the telencephalon territory of vertebrates and the palp forming territory of ascidians as some links have been proposed between these two developmental territories (e.g. line 78).

[Reviewer's comments]

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

Summary. The manuscript presents a detailed examination of how dynamic changes in BMP signaling during the development of the ascidian larval palps. Early in development BMP inhibition is responsible for the formation of a large field within the neuroectoderm that includes, among other fates, the presumptive palps. As development progresses, the territories of BMP activity/inhibition appear to be spatially refined within the palp-forming territory to specify palp versus interpalp fate. The experiments are presented with sufficient replication and statistical rigor.

[Response]

We thank the reviewer for the evaluation of our work.

Major Comments.

1. The researchers should look at otx expression in pFOG>Admp overexpressing embryos. It is difficult to assess from Figure 1, but it appears possible the the entire anterior sensory vesicle (not just the palps) are absent in the pFOG>Admp embryos (can the authors say briefly whether other ectodermal structures such as the atrial primordia or the oral siphon are still present?). Thus, is it possible that the entire a-lineage is disrupted? This would be an important distinction to make: are the defects attributed to experimental BMP activation specific to the palps, or are they more widespread in the anterior neuroectoderm? If the entire a-lineage is mis-fated, might this change the interpretation of the role of BMP inhibition? For example, might the formation of the palps depend on the proper development of the neighboring anterior neural plate? To address this concern, the authors should use a different driver to restrict Admp overexpression only to the palp forming region.

[Response]

In Figure 1, we show that Celf3/4/5/6, a general neural marker was still expressed in pFog>Admp embryos. We explain, in the Figure 1 legend, that this most likely corresponds to the CNS. It does not demonstrate that the anterior sensory vesicle (a-line induced CNS lineage) is still present. Unfortunately, Otx cannot be used as a suitable marker since it is also expressed in the posterior sensory vesicle (A-line lineage) (Hudson et al., 2003). Other a-line markers do exist. However, determining their expression at tailbud stages may not be conclusive since it is most likely that the patterning of the sensory vesicle (hence the expression of these markers) is modified after BMP activation. We have presented in former Figure 3 and Figure S1, strong evidence that the a-line neural lineage is intact at the neural plate stage. To better communicate these data, we have combined then in a modified Figure 3 that includes all markers examined and interpretative embryonic schemes. We show that, following BMP2 treatment, Otx and Celf3/4/5/6 were downregulated in the palp lineage but otherwise normal. Consequently, the a-line CNS lineage is most likely not affected by BMP pathway activation. This does not mean that its later derivatives form normally, but this is an issue that we have not addressed. A previous report indicates that BMP activation leads to Six1/2 repression and, possibly, the absence of oral siphon primordium (based on the images, no description in this paper) (Figure 1 from Abitua et al., 2015).

We think that we have addressed the concern of the reviewer, but would like to comment on the suggested experiment. It is very difficult to find a driver that would allow BMP activation only in the palp lineage (by overexpressing a constitutive active BMP receptor for example). a-line neural linage and palp lineage are intimately linked and separate at gastrula stages (St. 10). The regulatory sequences of Foxc, the first palp specific gene that we know, would thus be interesting. But it is most likely too late according to our whole embryo protein treatments (Figure 4). In agreement with this assumption, overexpressing Bmp2/4 (another BMP ligand) using the regulatory sequences of Dmrt (a master regulator of the palp+a-line CNS lineage expressed just before Foxc) does not apparently abolish palp formation (Extended Data Figure 5 from Abitua et al., 2015).

1. The authors hypothesize that papilla versus inter-papilla fate is controlled by differential BMP signaling. Is it possible to show differential P-Smad staining in papilla versus inter-papilla territories, as in Figure 2 for earlier gastrula-stage embryos? This data would make the authors hypothesis much more compelling. It appears that the authors have the necessary reagents.

[Response]

The actual lineage and fate segregation of papilla and inter-papilla lineage has not been determined as far as we know. Our current understanding comes from indirect evidence from gene expression and gene function, in particular from the study of Foxg and Sp6/7/8/9 by Liu and Satou (2009). Papillae originate from the 3 Foxg/Isl positive spots that are visible at very early tailbud stages. At earlier stages, Isl is not expressed and Foxg is expressed with a U-shape (Figure 5). Within this U, it is most likely that the segregation of papilla and inter-papilla fates takes place when Sp6/7/8/9 starts being expressed at late neurula stages. It is thought that Sp6/7/8/9+/Foxg+ cells will become inter-papilla cells while Sp6/7/8/9-/Foxg+ will become papilla. Our data indicate that BMP signaling is active in the future ventral papilla. We have mapped these data on schematics in the modified Figure 2.

Minor Comments.

1. There is no mention of panels Figure 1 U and V in the text. In the figure legend they are misidentified as panels S and T.

[Response]

This has been corrected.

Very small issue with English usage that occurs throughout the manuscript. The authors should check the use of "palps" versus "palp", particularly when expressions such as the following are used: "palps formation", "palps network", "palps lineage", "palps differentiation", "palps molecular markers", "palps neuronal markers", "palps phenotypes", etc . For example, the sentence, "Here, we show that BMP signaling regulates two phases of palps formation in Ciona intestinalis", should read instead "Here, we show that BMP signaling regulates two phases of palp formation in Ciona intestinalis".

[Response]

Thank you, we have corrected these mistakes.

It would be worth mentioning possible relationships between the tunicate palps and the adhesive glands for larval fish and amphibians. Are there common mechanisms? All of these are anterior ectoderm derivatives.

[Response]

Thank you for the suggestion. We have added a section on that topic in the discussion (line 358).

Please consider providing references in the Introduction for the sentences which end on the following lines of text: 36 ( . . . is the sister group of vertebrates), 46 ( . . . and sensory properties), 48 ( . . . the secretion of adhesive materials), 57 ( . . . on the nervous system in chordates), 68 ( . . . also known as Ap2-like), 74 ( . . . anterior neural territories)

[Response]

References have now been added.

To provide extra emphasis and to help the figures to stand alone with their respective legends, can you mention in the legend for Fig. 2 that D and E are controls? Also, can a brief legend be provided for S2 to give overall indication of staging, scale, orientation, etc.?

[Response]

Actually, the original Fig 2D and 2E correspond to treated embryos as explained in the legend. For clarity, these embryos have been separated from control embryos in the modified Figure 2.

Figure S2 has modified and a legend has been added.

Reviewer #2 (Significance (Required)):

Significance.

This study presents an advance in our understanding of the fine-structure regulation of BMP signaling in sculpting neuroectoderm derivatives. While this study is potentially of broad interest, the authors fail to fully discuss the comparative aspects of this study in the context of conserved chordate developmental mechanisms. This could be remedied without too much difficulty in the Discussion section.

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

Summary: This paper explores the role of BMP signaling for palp formation in ascidians using gain and loss of function approaches. The paper shows that while BMP at early (gastrula) stages prevents formation of the Foxc-positive palp ectoderm in Ciona, at later stages it appears to be essential for separation of the palps (possibly by promoting differentiation of interpapillary cells). The paper further shows that BMP plays similar roles in a different ascidian, Phallusia mammillata. Using previously published RNA-Seq results for the latter species after BMP up-regulation, the authors were able to identify additional BMP-responsive genes expressed in the palp region of ascidians.

[Response]

We thank the reviewer for the evaluation of our work.

Major comments: However, while the effect of BMP overexpression at early stages has been confirmed by two independent strategies (electroporation of the BMP agonist ADMP and BMP2 treatment), the effects of late BMP activation as well as the effects of BMP inhibition at both early and late stages have been studied exclusively by pharmacological treatments with a single BMP signaling agonist (BMP2) and antagonist (DMH1). To substantiate these findings and rule out unspecific side effects, it would have been desirable to verify them with alternative strategies.

[Response]

The reviewer may have missed some of our data. We have shown that BMP inhibition through overexpression of the secreted antagonist Noggin via electroporation using the early ectodermal driver pFog gives the same phenotypes as DMH1 treatment. The effects on Foxc * were presented in Figure S1, and are now presented in the modified Figure 3 (line 170). We also showed that the morphological Cyrano phenotype was observed with Noggin overexpression (modified Figure 6H). We now present a novel Figure S1 with expression of Isl and Celf3/4/5/6* following Noggin overexpression, and stress the use of this independent way of inhibiting BMP (lines 260-264). Given that early or late BMP inhibition lead to the same phenotype, we do not consider that overexpressing Noggin at gastrula stages is necessary.

Regarding BMP activation from gastrula stages, we have only used BMP2 treatment. It may be possible to overexpress Admp using promoters active in the palp lineage such as the ones of Dmrt, Foxc or Foxg. However, it may be difficult to phenocopy the phenotype obtained using BMP2 protein (loss of ventral palp), for two reasons. First, the precise timing to reach high BMP activation is not tightly controlled using such a method. Hence, all drivers should be tested. Second, the different promoters are active progressively later in development and in more and more restricted regions. Consequently, we consider that this requires a huge effort to validate a method (BMP protein treatment) that we already validated for the early effects and that has been used in several publications.

Therefore, while this study provides some new insights into the role of BMP in the specification of the palp forming region and subsequent palp development in ascidians, the evidence provided is relatively weak. Moreover, the scope of the study is quite limited. While identifying some BMP-responsive genes expressed in the palp region and describing the effects of BMP dysregulation on palp morphology, the study does not provide further insights into the underlying mechanisms how BMP patterns this region or affects subsequent palp formation.

[Response]

We are surprised by the appreciation of the reviewer describing our work as 'some new insights'. To our knowledge, this is the first report addressing the role of BMP signaling in palp formation at the molecular level. The only previous report by Darras and Nishida (2001) describes solely the morphology of the palps following overexpression of Bmp2/4 and Chordin overexpression by mRNA injection. We have brought significant novel findings 1) two important steps in palp formation with a precise description of the cellular and molecular actors, and a proposed function for BMP at each step, 2) evidence for conservation of this process in different ascidian species and 3) significant enrichment in the molecular description of this process. Moreover, the reviewer does not ask for specific items, we thus feel in the impossibility to offer satisfaction.

Minor comments:

• 63: ...as the anterior...

[Response]

Corrected.

• 68, 71, 74: references missing

[Response]

References have now been added.

• 73: better: anterior neural territories and placodes

[Response]

Corrected.

• 76: palp territories also share molecular signature with anterior (eg. olfactory) placodes, not only telencephalon

[Response]

Corrected.

• 106: awkward sentence

[Response]

Corrected.

• 114: at what stage was ADMP electroporated?

[Response]

Electroporation of plasmid DNA is performed in the fertilized egg. Transcription of the transgene is controlled by the driver. In this case, with pFog, it occurs from the 16-cell stage. This precision has been added in line 121.

• 134: to facilitate comparison between stages it would be useful to label cells in Fig. 2(eg. which are a-line and b-line cells? Where is the border between them?)

[Response]

As suggested by the reviewer, we have modified Figure 2 with embryo outlines and schemes to better appreciate where BMP signaling is active.

• 152: since Foxc and Foxg overlap with pSMAD1/5/8 at neurula but not gastrula stages, do you know whether this is due to a dorsal expansion of BMP activity or a ventral expansion of Foxc/Foxg expression? Again, labeling of the nuclei would help

[Response]

The change corresponds to a dorsal expansion of P-Smad1/5/8. Our conclusion comes from combining nuclear staining (not shown for simplicity) and available fate maps. The results are presented in schematic diagrams of embryos in frontal views in the modified Figure 2.

• 174: the description is not clear here; what proportion of embryos did show reduction versus expansion of expression?. Why is the reduction shown in Fig.3 D asymmetrical?

[Response]

The proportions are now indicated in line 184.

We apologize for the impression led by Fig 3D. Actually, it was the only case where the embryo was shown from the side (the description as a lateral view was inadvertently omitted in the legend). It did not show an asymmetric repression but an ectopic expression. We have now modified Figure 3 by properly showing only dorsal (neural plate) views and lateral views in insets when necessary. In addition, we have added schemes of embryos depicting the main tissues we have examined (palps, CNS and epidermis) and their localization depending on the treatments. We hope that the results are now clearly presented.

• 198: ... of endogenous...

[Response]

Corrected (line 213).

• 208: I suggest to highlight the regions of changes in Fig. with asterisks/arrows etc.

[Response]

We have added schematic embryos to highlight expression changes in the modified Figure 5.

• 218: contrary to what is stated here, there is no depiction of u-shaped Isl1 expression in control embryos of Fig. 4

[Response]

As also pointed by reviewer 1, we apologize for the misunderstanding since the sentence was not clear. We referred to the U-shaped Isl expression under BMP inhibition. Indeed, Isl starts to be expressed in 3 separate domains in the palp forming region, and not following a U-shape as its upstream regulator Foxg (Liu and Satou, 2019). We amended the sentence (lines 234-235).

• 220: the cell shapes referred to here cannot be seen in Fig. 4 (too small)

[Response]

We have modified Figure 6 to include close up of the palps.

• 271: the description here is confusing: first you talk about 53 genes and the mention palp expression of 12/26. Where does number 26 come from? And why was in situ done then for 27 additional genes? Also, while the comparison with previously published RNA-Seq data was valuable in uncovering additional BMP-sensitive palp markers, it does not provide any substantial new insights into how BMP patterns this territory.

[Response]

We have amended the sentence to make it clearer (lines 291-295).

• line 624: where

[Response]

Thank you. Corrected line 731.

• Fig. 2: to facilitate comparison between stages it would be useful to label cells (eg. which are a-line and b-line cells? Where is the border between them?)

[Response]

Already responded above.

-Fig. 3: Why is the expression in D asymmetrical? In the main text you write that expression is expanded in some embryos but reduced in others - Please show examples also of the expanded phenotype and give numbers

[Response]

Already responded above.

• Fig. 6: small panels in I, L, N need to be explained (single channels), white signal needs to be explained (overlap ?)

[Response]

We used white for better display of separate single channels. Given the confusion and the good quality of the 2 color fluorescent in situ images, we removed these panels in the modified Figure 6.

White in K and L correspond to overlap (explained in the legend).

• Fig. S2: legend is missing

[Response]

This has been amended.

Reviewer #3 (Significance (Required)):

Since the study does not provide substantial new insights into the mechanisms how BMP patterns the palp forming region or affects subsequent palp formation in ascidians, it will be of interest mostly for a specialized audience in the field of developmental biology.

[Response]

We do not agree with the reviewer as discussed above. The description of the role of BMP signaling in the specification of the ANB and its subsequent patterning in ascidians has interesting evolutionary implications and should be of interest for a broader audience.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This paper explores the role of BMP signaling for palp formation in ascidians using gain and loss of function approaches. The paper shows that while BMP at early (gastrula) stages prevents formation of the Foxc-positive palp ectoderm in Ciona, at later stages it appears to be essential for separation of the palps (possibly by promoting differentiation of interpapillary cells). The paper further shows that BMP plays similar roles in a different ascidian, Phallusia mammillata. Using previously published RNA-Seq results for the latter species after BMP up-regulation, the authors were able to identify additional BMP-responsive genes expressed in the palp region of ascidians.

Major comments:

However, while the effect of BMP overexpression at early stages has been confirmed by two independent strategies (electroporation of the BMP agonist ADMP and BMP2 treatment), the effects of late BMP activation as well as the effects of BMP inhibition at both early and late stages have been studied exclusively by pharmacological treatments with a single BMP signaling agonist (BMP2) and antagonist (DMH1). To substantiate these findings and rule out unspecific side effects, it would have been desirable to verify them with alternative strategies.

Therefore, while this study provides some new insights into the role of BMP in the specification of the palp forming region and subsequent palp development in ascidians, the evidence provided is relatively weak. Moreover, the scope of the study is quite limited. While identifying some BMP-responsive genes expressed in the palp region and describing the effects of BMP dysregulation on palp morphology, the study does not provide further insights into the underlying mechanisms how BMP patterns this region or affects subsequent palp formation.

Minor comments:

• 63: ...as the anterior...
• 68, 71, 74: references missing
• 73: better: anterior neural territories and placodes
• 76: palp territories also share molecular signature with anterior (eg. olfactory) placodes, not only telencephalon
• 106: awkward sentence
• 114: at what stage was ADMP electroporated?
• 134: to facilitate comparison between stages it would be useful to label cells in Fig. 2(eg. which are a-line and b-line cells? Where is the border between them?)
• 152: since Foxc and Foxg overlap with pSMAD1/5/8 at neurula but not gastrula stages, do you know whether this is due to a dorsal expansion of BMP activity or a ventral expansion of Foxc/Foxg expression? Again, labeling of the nuclei would help
• 174: the description is not clear here; what proportion of embryos did show reduction versus expansion of expression?. Why is the reduction shown in Fig.3 D asymmetrical?
• 198: ... of endogenous...
• 208: I suggest to highlight the regions of changes in Fig. with asterisks/arrows etc.
• 218: contrary to what is stated here, there is no depiction of u-shaped Isl1 expression in control embryos of Fig. 4
• 220: the cell shapes referred to here cannot be seen in Fig. 4 (too small)
• 271: the description here is confusing: first you talk about 53 genes and the mention palp expression of 12/26. Where does number 26 come from? And why was in situ done then for 27 additional genes? Also, while the comparison with previously published RNA-Seq data was valuable in uncovering additional BMP-sensitive palp markers, it does not provide any substantial new insights into how BMP patterns this territory.
• line 624: where
• Fig. 2: to facilitate comparison between stages it would be useful to label cells (eg. which are a-line and b-line cells? Where is the border between them?) -Fig. 3: Why is the expression in D asymmetrical? In the main text you write that expression is expanded in some embryos but reduced in others - Please show examples also of the expanded phenotype and give numbers
• Fig. 6: small panels in I, L, N need to be explained (single channels), white signal needs to be explained (overlap ?)
• Fig. S2: legend is missing

Significance

Since the study does not provide substantial new insights into the mechanisms how BMP patterns the palp forming region or affects subsequent palp formation in ascidians, it will be of interest mostly for a specialized audience in the field of developmental biology.

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Referee #2

Evidence, reproducibility and clarity

Summary.

The manuscript presents a detailed examination of how dynamic changes in BMP signaling during the development of the ascidian larval palps. Early in development BMP inhibition is responsible for the formation of a large field within the neuroectoderm that includes, among other fates, the presumptive palps. As development progresses, the territories of BMP activity/inhibition appear to be spatially refined within the palp-forming territory to specify palp versus interpalp fate. The experiments are presented with sufficient replication and statistical rigor.

Major Comments.

1. The researchers should look at otx expression in pFOG>Admp overexpressing embryos. It is difficult to assess from Figure 1, but it appears possible the the entire anterior sensory vesicle (not just the palps) are absent in the pFOG>Admp embryos (can the authors say briefly whether other ectodermal structures such as the atrial primordia or the oral siphon are still present?). Thus, is it possible that the entire a-lineage is disrupted? This would be an important distinction to make: are the defects attributed to experimental BMP activation specific to the palps, or are they more widespread in the anterior neuroectoderm? If the entire a-lineage is mis-fated, might this change the interpretation of the role of BMP inhibition? For example, might the formation of the palps depend on the proper development of the neighboring anterior neural plate? To address this concern, the authors should use a different driver to restrict Admp overexpression only to the palp forming region.
2. The authors hypothesize that papilla versus inter-papilla fate is controlled by differential BMP signaling. Is it possible to show differential P-Smad staining in papilla versus inter-papilla territories, as in Figure 2 for earlier gastrula-stage embryos? This data would make the authors hypothesis much more compelling. It appears that the authors have the necessary reagents.

Minor Comments.

1. There is no mention of panels Figure 1 U and V in the text. In the figure legend they are misidentified as panels S and T.
2. Very small issue with English usage that occurs throughout the manuscript. The authors should check the use of "palps" versus "palp", particularly when expressions such as the following are used: "palps formation", "palps network", "palps lineage", "palps differentiation", "palps molecular markers", "palps neuronal markers", "palps phenotypes", etc . For example, the sentence, "Here, we show that BMP signaling regulates two phases of palps formation in Ciona intestinalis", should read instead "Here, we show that BMP signaling regulates two phases of palp formation in Ciona intestinalis".
3. It would be worth mentioning possible relationships between the tunicate palps and the adhesive glands for larval fish and amphibians. Are there common mechanisms? All of these are anterior ectoderm derivatives.
4. Please consider providing references in the Introduction for the sentences which end on the following lines of text: 36 ( . . . is the sister group of vertebrates), 46 ( . . . and sensory properties), 48 ( . . . the secretion of adhesive materials), 57 ( . . . on the nervous system in chordates), 68 ( . . . also known as Ap2-like), 74 ( . . . anterior neural territories)
5. To provide extra emphasis and to help the figures to stand alone with their respective legends, can you mention in the legend for Fig. 2 that D and E are controls? Also, can a brief legend be provided for S2 to give overall indication of staging, scale, orientation, etc.?

Significance

This study presents an advance in our understanding of the fine-structure regulation of BMP signaling in sculpting neuroectoderm derivatives. While this study is potentially of broad interest, the authors fail to fully discuss the comparative aspects of this study in the context of conserved chordate developmental mechanisms. This could be remedied without too much difficulty in the Discussion section.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this article Roure et al address the role of BMP during formation of the ascidian palps, using Ciona intestinalis. Overexpression of BMP (specifically ADMP) from early stages of development results in complete suppression of palp formation, and early loss of the palp forming region (also called anterior neural border ANB). Using p-Smad1/5/8 antibody staining they show a marker of the ANB (FoxC) is expressed in a region negative for BMP signals. Inhibition of BMP signals is not sufficient to produce ectopic ANB. However, treatment with FGF protein from very early stages (8-cell stage) plus inhibition of BMP signaling (from 8-cell stage) increased FoxC expression. Looking at later stages of development the authors show that in a U-shaped expression domain of Foxg, Smad1/5/8 is active in the ventral-most part, which is expected to form the ventral-most palp. BMP2 treatment from gastrula stages results in loss of the ventral most palp expression of Isl and repression of ventral Foxg expression. Inhibition of BMP signaling from gastrula or neurula stages results in failure of a U-shaped pattern of Isl expression to resolve into the three palp expression domains, and by late tailbud stages, Sp6/7/8/9 (proposed as a repressor of Foxg in the inter-palp territory) expression is reduced and the numbers of specific cell-types making up the palps is increased. These cells are present in a single large palp of dorsal identity. Thus, inhibition of BMP from early gastrula stages results in a single palp made of more cells than the three palps of control larvae, presumably due to recruitment of cells usually present between the palps.

The authors then show a similar phenotype in another ascidian species Phallusia mammillata. Using their previous RNA-Seq data of embryos treated with BMP4, they looked for potential novel palp markers and identify a further eight novel markers of the palps. Looking further into this data and at a list of 68 genes expressed in palps (but not exclusively) they find that in whole embryo RNA-Seq data 70% were regulated by BMP signaling, mostly repressed, but some activated by BMP. 30 of these genes were regulated by Notch.

Apart from the confusion I explained in my comments below, the data seems to be carefully presented and interpreted. Overall, this manuscript presents a more detailed analysis of the role of BMP signaling during ascidian palp formation, but it remains to be precisely understood.

Major comments

1. I am a little confused about the timing of the protein treatments. In Figure 2, the authors show nicely that at the neurula stages, P-Smad1/5/8 staining abuts the FoxC ANB territory. Then at late neurula P-Smad1/5/8 is detected in the ventral-most part of the Foxg U-shaped part of the palp forming region, presumably the ventral most palp. However, the protein treatments with BMP (and FGF) are carried out from the 8-cell stage, which seems a bit drastic and embryos look difficult to orientate (e.g. Fig. 3D). While BMP-treatment from early stages inhibits all palp gene expression and any sign of palp formation (Figure 1), treatment with BMP from the early gastrula stage, when Smad1/5/8 is detected only in mesendoderm cells and before it is detected in any ectoderm, is sufficient only to block ventral palp formation and cause a partial down-regulation of FoxC expression in the ANB. Thus, there seems to be a discrepancy between the roles proposed for BMP during ANB and palp formation as judged by P-Smad1/5/8 staining and the temporal evidence from BMP- and BMP-inhibitor treatment. Do the authors have some explanation for why they need to treat at least one hour before the BMP-mediated patterning mechanism (as indicated from the P-Smad1/5/8 staining) is taking place? For example, could the authors check how long it takes DMH1 to inhibit P-Smad1/5/8 positive staining? Or BMP to strongly induce P-Smad1/5/8? This seems to be a simple experiment and might go some way to explaining why they need to treat embryos much earlier than I would have thought necessary.
2. It does not make sense to me that BMP treatment from gastrula stage blocks only ventral palp formation (Figure 4) and ventral Foxg expression (Fig. 5G). In particular, it is the ventral palp region which is positive for P-Smad1/5/8 (Fig.2I,J) so I would not expect the ventral palp to be the most sensitive to BMP-treatment.

Minor comments

line 185 I see what the authors are trying to say but I don't agree that BMP limits the domain of FoxC expression as inhibition of BMP has no effect on FoxC. Rather BMP has to be kept out of the ANB in order to allow ANB formation.

The relationship between Foxg and Sp6/7/8/9 expression is not really clear and it would be better to do this with double ISH if the authors want to show mutually exclusive expression domains, or at least provide a summary figure.

Line 218, I do not see the data showing that Isl is expressed at a U-shape at st. 23, it seems to be expressed in three dots, unless embryos are treated with DMH1.

Figure 6B, G. It could be nice to show a close up of the palps to see elongated cells.

Figure 6K. It is better to use a statistical test to support the authors conclusions.

It could be nice to provide a timeline for Smad1/5/8 signaling and the role for BMP signals that are proposed in this manuscript as a summary diagram.

lines 66-74 is lacking references.

Significance

While it is still not clear how BMP signals are established (which ligands for example) and their precise role in palp formation, this manuscript adds more information to our current understanding of the role of BMP signaling during palp formation. In particular it shows that BMP signals need to be kept out of the ANB for its formation and that it is required to resolve the later forming palp territory into three discrete palp regions. However, there is some way to go before this is fully understood. This article will certainly be of interest to ascidian developmental biologists trying to understand the formation and patterning of the larval PNS. It may also be of some interest to evolutionary biologists trying to understand the relationship between the telencephalon territory of vertebrates and the palp forming territory of ascidians as some links have been proposed between these two developmental territories (e.g. line 78).

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Reply to the reviewers

Reviewer 1

This paper identifies a role for the hereditary spastic paraplegia protein spatacsin in lysosome morphology, positioning and dynamics, and undertakes detailed mechanistic studies to try to identify the mechanism for this effect. In doing so the paper elucidates further mechanistic information about the properties of two other hereditary spastic paraplegia proteins, spastizin and AP5Z1. The work is done in mammalian cells and uses a combination of over-expression, depletion and biochemical studies. The main findings are:

1. The authors present evidence that spatacsin is an ER-localised protein.
2. Murine embryonic fibroblasts lacking spatacsin have a reduced number of tubular lysosomes and the remaining lysosomes are less motile. In general, a relationship between tubular lysosome morphology and lysosome motility, often in association with the endoplasmic reticulum (ER), is demonstrated. These tubular lysosomes are catalytically active and acidic.
3. In terms of mechanism of this effect, by combining a yeast-two hybrid and siRNA phenotypic screen, the authors identify a number of spatacsin-interacting proteins that also regulate lysosomal tubulation. The most important of these for the purposes of this paper is UBR4, an E3 ubiquitin ligase.
4. The authors show that spatacsin and UBR4 promote degradation of AP5Z1, and that this property required the ability of spatacsin to interact with UBR4. Somewhat surprisingly, as AP5Z1 is a coat protein, this degradation appeared to occur within the lumen of the lysosome - the authors speculate how this could be in the discussion.
5. The authors then demonstrate that AP5Z1 and spastizin, both hereditary spastic paraplegia proteins, compete for binding with spatacsin.
6. The relationship between spatacsin, spastizin, AP5Z1 and motor proteins in then examined. There is a known interaction between spastizin and KIF13A and expression of a dominant negative KIF13A protein reduced lysosomal tubulation. The authors then demonstrate an interaction between AP5Z1 and the p150Glued dynein/dynactin complex member, then showed that expression of a dominant negative p150Glued protein reduced lysosomal tubulation.
7. Finally, that authors demonstrate the relevance of these findings to neurons, the target cells of hereditary spastic paraplegia, by showing that lysosomal tubulation and axonal transport are reduced in mouse neurons lacking spastacsin, and that depletion of UBR4 or AP5Z1 affected these as expected from the experiments above.

Major comments:

Overall I believe that the key conclusions of this paper are generally convincing and that the work is of high quality. However, I do have some reservations:

1. The localisation of spatacsin on the ER. It is always difficult to be convinced about colocalization of a diffuse punctate marker and the ER. From the STED experiments in figure 1, while it definitely seems that there is some spatacsin on the ER, there also appears to be some spatacsin puncta that are not. I'd like to know if these puncta represent lysosome-associated spatacsin. This is important for interpretation of the subsequent experiments (see point 3 below). I also think quantification of these co-localisation will increase confidence in the results. In addition, a caveat of the immunofluorescence studies is that they use over-expressed spatacsin. I appreciate that there are no good antibodies to endogenous spatacsin, but I don't think this limitation is sufficiently acknowledged. As the claim of ER-localisation is critical for the proposed mechanistic model, and in the absence of experiments with endogenously tagged spatacsin, this makes the biochemical fractionation studies of figure 1C very important. To make these more convincing I would prefer to see additional control markers to verify the separation of lysosomal and ER compartments - e.g. lamp1, lamp2, an ER tubular marker such as a REEP5 or a reticulon.

Authors response : We agree with the reviewer that the localization of spatacsin is critical, and we appreciate the knowledge of the reviewer concerning the lack of good antibodies to endogenous spatacsin. We better acknowledged this limitation in our revised manucript (p. 5 and p. 15). We performed extra experiments to convincingly show that spatacsin is indeed localized at the ER. First, we performed 3-color STED experiments to visualize in the same cell spatacsin, the ER and lysosomes. The preliminary data seem to indicate that some spatacsin is associated with lysosomes at ER-lysosomes contact site. We plan to add quantifications of colocalization between spatacsin and ER staining at STED resolution to better support the fact that spatacsin is a protein of the ER.

Moreover, as requested, we have performed a western blot with Lamp2 and REEP5 antibodies on the ER- and lysosome-enriched fractions (New Figure 1B). This western blot shows that a significant proportion of Lamp2 is present in the ER-enriched fraction, which may be explained by the strong association of ER with late endosomes and lysosomes. Yet the lysosome-enriched fractions that contained no ER markers do not present spatacsin staining, suggesting that spatacsin is either in the ER or in lysosomes associated with the ER that are not positive for cathepsin D. We reformulated the text of Figure 1 according to the new included data (p. 5-6).

The authors generally do a good job of quantifying their results. However, this is lacking for the biochemical experiments (immunoblotting and IP) in figures 4 and 5, and I would prefer to see these quantified (the quantification should include data from repeat experiments so that we can judge the reproducibility of the results).

Authors response : We agree that our presentation did not indicate that the western blots were repeated several times. We have added quantifications for the western blots present in Figures 4 and 5.

On page 10, referring to the proximity ligation results, the authors comment: "This suggests that the spatacsin-spastizin interaction occurs at contact sites between the ER and lysosomes to allow spastizin recruitment to lysosomes". I'm not sure this statement is fully supported, as mentioned at point 1 above it is possible that some steady state spatacsin is at lysosomes. To fully support this, we'd need to see the PLA signal also convincingly co-localise with an ER marker.

Authors response : We will perform extra PLA experiment to indeed show that the spots where spatacsin and spastizin colocalize with an ER marker. This data will be added in Figure 5.

In figure 6C and D the effect of spastizin on lysosomal tubulation and dynamics is investigated. Wartmannin treatment is used to do this, as it is known to remove spastizin from lysosomes. However, this is a very indirect manipulation that could have many other consequences and it would be better to demonstrate this directly by showing the effect of depletion of spastizin on lysosomal morphology/dynamics. I also think the role of AP5Z1 in tubulation/dynamics would be better supported with additional experiments to deplete the protein - at present only over-expression is examined.

Authors response: *We added new data to answer this comment. Downregulation of spastizin using siRNA led to lower number of tubular lysosomes and decreased the proportion of dynamic lysosomes, showing that spastizin is required to regulate lysosome motility (Figure 6B-6C Supplementary Figure 7B). We have also added new data regarding downregulation of AP5Z1 (Figure 6A-6C-Supplementary 7A). Both overexpression and downregulation of AP5Z1 using siRNA decreased the number of tubular lysosomes and decreased the proportion of dynamic lysosomes (Figure 6A-6C-Supplementary Figure 6C-D). *

This observation suggests that the levels of AP5Z1 must be tightly regulated to control lysosome motility. We added discussion about this point as well (p.12-13).

While the experiments showing that over-expression of dominant negative forms of KIF13A and p150Glued affect lysosomal tubulation/dynamics provide good circumstantial evidence that spatacsin influences these lysosomal properties via its interactions with spastizin and AP5Z1 (which bind to these motor proteins), the authors have not shown that the interaction of the motor proteins with spastizin and AP5Z1 is required for this ability to regulate lysosome tubulation/dynamics. This means that the model presented in figure 7 is not fully supported by the data. If the authors have been able to map the binding regions for these interactions then perhaps this could be investigated with rescue experiments, although I appreciate that this is potentially a major piece of work and perhaps outside the scope of this paper. An alternative would be that the authors acknowledged this part of the model as somewhat speculative.

Authors response : We agree with the reviewer that our data do not show that KIF13A and p150Glued interact directly with spastizin and AP5Z1 to regulate lysosome dynamics. It has previously been shown that the adaptor complex AP2 interacts with p150glued via the ear domain of AP2 b subunit (Kononenko et al, 2017). It is therefore likely that the interaction of adaptor complex 5 with p150-Glued also occurs via AP5B1 subunit, and thus interaction of AP5Z1 with p150 glued would be indirect. *We discussed this point carefully (p.16). *

*Regarding the interaction of Spastizin with KIF13A, it was identified by yeast-two hybrid screen and validated by GST-pulldown (Sagona et al, 2010). This showed that KIF13A interacts with the C-terminal domain of Spastizin, and we discussed this point. To confirm that KIF13A interaction with spastizin is required to promote its role in tubular lysosome formation and dynamics, we can perform an experiment where we downregulate endogenous mouse spastizin using siRNA and express either full length human spastizin to rescue the effect of the siRNA, or overexpress a human spastizin lacking its C-terminal domain required for the interaction with KIF13A (where we would expect no rescue). This would strengthen our conclusion on the role of KIF13A in link with spastizin to regulate the formation and dynamics of tubular lysosomes. We could add these data in Figure 6 (or Supplementary Figure 7). *

• Are the experiments adequately replicated and statistical analysis adequate?

In general I am not convinced that the statistical tests are applied rigorously in this paper. Most experiments are done three times, but the "n" used for statistical testing is typically chosen as, e.g. the number of cells, number of lysosomes, rather than number of biological repeat experiments. This means that inter-experimental variability is not rigorously taken into account. A more rigorous practice would be to use the mean measures for each of three biological repeats and apply the statistical tests to the three means, so n=3 if three repeats were done. Superplots would be a nice way to graphically display these data.

Authors response : We agree with the comments of the reviewer regarding data presentation. We have therefore changed the presentation of all graphs of the manuscript using superplots that allow us to show all the points that were analyzed as well as the mean value for each biological replicate, and performed statistical analyses by comparing the biological replicates as proposed in Lord et al, JCB 2020 (10.1083/jcb.202001064).

Minor comments:

1. In supplementary figure 3D I cannot honestly say that I see the smaller band.

Authors response : We agree that this western blot is not clear. We will provide a new western blot.

When first called out, I expected supplementary tables 1 and 2 to show the list of interactors with wild-type spatacsin and spatacsind32-34 respectively, but this is not what they show.

Author response : We have added two supplementary data tables (Now Supplementary Tables 1 and 2) to give the list of interactors of wild-type C-terminal domain of spatacsin and spatacsinD32-34, respectively.

Supplementary Tables 3 and 4 now refer to the analysis of the downregulation experiments by respectively the neural network method and the tubular lysosome detection method.

The experiments in Figure 4A are a little problematic in the way that they are called out. The first call refers to just a small subset of the data in the figure, and the figure is then called out at various points later in the paper. This is quite confusing. Is there any way this could be simplified?

Authors response :We agree with the reviewer that Figure 4A was called at various points of the manuscript. This was to avoid duplicating data into two separate figures. However, we have modified the presentation of Figure 4 and Figure 5. We have included new Figure 4C to show that downregulation of UBR4 prevents the degradation of AP5Z1 upon overexpression of Spatacsin-GFP, but also in basal conditions in wild-type fibroblasts. The co-IP that was originally presented in Figure 4A has now been moved into Supplementary Figure 6A.

The section on page 10: "Spatacsin also interacts with spastizin, and is required to recruit spastizin to lysosomes (Hirst et al., 2021). ........ We hypothesized that spatacsin interaction with spastizin was required for spastizin localization to lysosomes." Is odd, as the authors seem to be hypothesising an observation that they have just said has already been demonstrated.

Authors response : We agree that these sentences were odd. We have rephrased the paragraph (p. 11).

Can the authors explain why there is so little interaction between wild-type KIF13A and spastizin?

Authors response : The interaction domain of spastizin with KIF13A is close to the motor domain according to the two-hybrid data published by Sagona et al (2010). The dominant negative construct of KIF13A that is devoid of the motor domain (KIF13A-ST) may thus facilitate access of spastizin to binding domain. We have commented on this point in the text (p.13).

In figure 6G p150Glued signal is also present in the control IP lane, which casts doubt on the specificity of the interaction. Could the authors generate a cleaner result?

Authors response : We have repeated the experiment 3 times, always with some p150Glued signal present in the control IP. Of note, as stated in the method section, we have increased the concentration of NaCl in the washing of this co-IP to decrease non-specific binding of p150glued to control beads, but we could not get cleaner results so far. We will try to get cleaner western blot to illustrate Figure 6G.

I would be interested to see how AP5Z1 expression differs between neurons with and without spatacsin- we would expect similar results to those shown in the MEFS.

*Authors response : We have not checked the levels of AP5Z1 in neurons with and without spatacsin yet. However, the complete knockout of spatacsin strongly modifies the levels of its partners. We previously showed that spastizin levels are decreased by >90% in Spg11 knockout brain (Branchu et al, 2017). Furthermore, the levels of AP5Z1 have been shown to be decreased by ~50% in fibroblasts of SPG11 and SPG15 patients (Hirst et al, 2015). *

*Our work shows that spatacsin promotes the degradation of AP5Z1 by lysosomes. It is possible that other degradation mechanism(s) may exist and could explain the lower levels of AP5Z1 in knockout cells. We discussed this point (p.15). *

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

In this study Pierga et al. report that SPG11 (spatacsin) is an ER-resident protein involved in the regulation of ER-lysosome contact sites (in particular tubular lysosomes) and subsequent faster motility of tubular lysosomes, as well in the degradation of AP5Z1 (SPG48), which forms a heterotrimeric complex with SPG15 (spastizin) and SPG11. This complex has been localized by several groups on the cytoplasmic side of LAMP-1-positive lysosomes. In addition, mutations in SPG11, SPG15, and SPG48 patients share various clinical features and were supported by biochemical/cell biological data from Spg11 and Spg15 KO mouse models and cultured cells both from patients and mice, respectively, demonstrating e.g. accumulation of autolysosome storage material, defects in the autophagic lysosome reformation process, and the loss of cortical motoneurons and Purkinje cells.

Major concerns:

i) Fig. 1, 2, 3: major disadvantage of this study is the analysis of overexpressed proteins (SPG11-V5, GFP-Sec61, and Lamp1-mCherry) which might contribute to the observed strong expression of SPG11-V5 in the ER/ER-enriched fraction. The results should be compared with the endogenous expressed proteins.

Authors response :* As stated by reviewer 1, there are no good antibodies to endogenous spatacsin, and therefore we have to rely on expression of tagged spatacsin to study its localization by immunohistochemistry. For the colocalization with the ER, we stained the latter by GFP-Sec61 that is a widely used marker for this compartment. To confirm our results, we plan to try to perform new STED imaging with REEP5 antibody to stain the ER, and Lamp1 antibody to label lysosomes, avoiding overexpression of proteins to label the subcellular compartments. Furthermore, as it is not possible to localize endogenous spatacsin by immunostaining, we addressed its localization by biochemical fractionation and western blots comparing wild-type and Spg11 knockout samples. *

For Figure 2, the data presented were indeed obtained using transfection of Lamp1-mCherry. However, we confirmed our observation of Figure 2A using alternative staining of lysosomes (Lysotracker or loading of lysosomes with Texas-Red Dextran). We therefore think that our data presented in figure 2 are valid, and that the effect we observed on tubular lysosomes was not affected by expression of Lamp1-mCherry.

In Figure 3, the lysosome were labelled with Texas-Red Dextran, and thus all the data presented in figure 3 do not rely on overexpression.

In Fig. 1C the lack of the mature Cathepsin D form which is proteolytically generated only in lysosomes from the higher molecular mass precursor is misleading and should be related to presence of lysosomal membrane proteins.

Authors response: As requested, we have performed a western blot to show the lysosomal membrane protein Lamp2 on the ER- and lysosome-enriched fractions (Figure 1B). This western blot shows that a significant proportion of Lamp2 is actually present in the ER-enriched fraction, which may be explained by the strong association of ER with late endosomes and lysosomes previously described (Friedman et al, 2013). Yet the lysosome-enriched fractions that contained no ER markers do not present spatacsin staining, suggesting that spatacsin is either in the ER or in lysosomes associated with the ER. We reformulated the text of Figure 1 according to the new included data (p 5-6). The 3-colours STED experiment that we plan to perform to answer reviewer 1 comments will help discriminate between these possibilities.

Fig. 1D: the TEM image shows only a single lysosome and proposed ER contact zones in wt-MEFs without comparison with Spg11 KO MEFs (only in the quantification). Without double immunogold labeling of SPG11 (and their lack on SPG11 KO cell lysosomes) and known ER contact-site proteins this image and the conclusion are insufficient.

Authors response : We have added an image of a lysosome taken from a knockout fibroblast (Figure 1E). As stated above there are no good antibodies to spatacsin for immunostaining, so it will not be possible to perform double immunogold labelling. This prevents us from claiming that spatacsin is a protein enriched at contact site. We therefore modulated our result section and discussion accordingly (p.5-6 and p.16).

ii) The rationale for the selection of the deleted Spg11 region D32-34 is not clear. What are the symptoms of this Spg11 knock-in mouse? A more detailed description of the phenotype is required Is the phenotype including the accumulation of LC3-positive material similar to the phenotype of the SPG11 KO mouse which has been published by Varga et al.(2015) and Branchu et al. (2017) ? If not, is the new mechanisms reported here not so important?

Author response : We have added new data (Supplementary Figure 3E-F) showing motor and cognitive impairment in mice expressing truncating spatacsin, although the motor dysfunction is slightly less marked than in Spg11 knockout animals. We also checked for accumulation of autophagy markers. We did not use LC3, but p62 that labels substrates to be degraded by autophagy. We observed accumulation of p62 in Spg11 knockout and in Spg11D32-34/D32-34 mouse neurons (Supplementary Figure 3G). These data support the functional importance of the domain encoded by exons 32 to 34 of Spg11. We commented on this in the text (p.9).

iii) p8/Fig. 3F/Suppl.Fig.3F- the most important part of the manuscript: what are the parameters of lysosomal staining in images that were used to identify genes important for lysosome tubulation by the neural network?

Authors response : For screening in Figure 3, lysosomes were stained by loading fibroblasts with Texas-Red Dextran overnight, followed by a wash of at least 4 hours. The neural network was first trained to discriminate between control and Spg11-/- fibroblasts, using any parameters of the lysosomal staining, not necessarily lysosome tubulation. This is a completely unsupervised and unbiased method, but one of its drawbacks is that we do not know which parameters were used by the network to discriminate between control and Spg11-/- fibroblasts. Therefore, we validated the classification performed by the neural network on a data set independent from the training set before using it for the screening. We rephrased the paragraph to make it clearer (p.9).

I cannot understand how the authors predict the probability of the cell to be considered as an Spg11 KO fibroblast (why not as an Spg11 D32-34 knock-in fibroblast?) as the basis for the selection of interaction candidates.

Author response : The neural network was trained on sets of images obtained from wild-type and Spg11 KO fibroblasts, which were expected to represent extreme lysosomal phenotypes linked to spatacsin function. We could therefore predict the probability of cells to be considered as Spg11 KO, not as Spg11 *D32-34 fibroblasts. We clarified this in the text (p9). *

A simple statement that the neural network approach identified those genes is too weak and requires more convincing experimental data. It has to be shown at least for the 8 positive genes in both approaches how the siRNA treatments of these genes phenocopied the lysosomal changes and of course the effect of the downregulation on the protein level of their products both in wild-type control and Spg11 D32-34 knock-in MEF. The Suppl. Fig.3F is completely unclear. How were the Y2H interaction partner validated? Did the authors use the identified 8 interaction candidates as full length bait to demonstrate the interaction with the Spg11 exons 32-34 ?

Author response : The purpose of the siRNA screen was to quickly identify putative candidates important for the regulation of lysosome dynamics. We identified 8 candidates possibly implicated in lysosomes dynamics based on the two analysis methods. We have added in Supplementary Figure 4 C-D the effect of both siRNA on lysosomal function by the two methods of analysis compared to the effect of siSPG11. However, here we aimed to identify candidates and we do not claim that every one of these eight proteins were indeed implicated in the regulation of lysosome dynamics. We corrected the text, accordingly, stating that the products of the 8 identified genes are good candidates to regulate lysosomal function (p.10). We validated the role of one of the identified candidates, UBR4, and we showed that the UBR4 siRNA indeed downregulates the protein level (Figure 4C). We only validated the interaction of spatacsin Cter with UBR4 by co-immunoprecipitation (Figure 4B).

*For the 7 remaining candidates, full characterization would indeed be required to validate their role and elucidate their mechanisms of action, but this is out of the scope of this manuscript. *

p8/Fig.3F: the genes identified in both approaches have to be listed in the Fig. 3F-Table.

Authors response : We have added in new Figure 3F the list of the 8 candidate genes that could contribute to regulate lysosome function.

The GO process- ubiquitin-dependent protein catabolic process is neither positive for the neural network nor for the directed analysis but positive for both analyses? Please explain. Similarly, the GO process proteolysis involved in cellular protein catabolic process -is not positive for the neural network analysis but again positive for both analyses.

Authors response : We agree with the reviewer that Table 3F in its older version could be a bit confusing. GO analysis is based on “enrichment” of biological processes within a list of proteins. As we did not have the same number of proteins in the 3 analyses provided in original Table 3F, we got variability in the identified biological processes. To simplify, we have therefore chosen to present only the GO analysis for the 8 candidates that were most likely implicated in lysosomal dynamics according to our two analyses of the siRNA screen which is the most relevant for our study (new Figure 3G).

For Fig. 3G the mutant ubiquitin-K0 staining in wild-type MEF cells has to be shown as well as for the Spg11 ki/KO MEFs (+ quantification of the respective data)

Authors response : As stated by Reviewer 4, the expression of lysine-null ubiquitin may impact many different cellular pathways. We therefore removed this part of the data in order to simplify the manuscript (p.10)

iv) The interpretation of the Y2H-interactome analysis by the authors is hard to follow. They searched with the exon 32-34 cDNA for binding partner, selected 3 degradative GO processes and showed by overexpression of a mutant Ub-K0 plasmid in wild-type MEFs a decreased number of tubular lysosomes, as well as their dynamics (without showing the control data in Spg11 KO or ki-MEFs). Thus, poly-ub of proteins should be in some way responsible for a lysosomal phenotype of Spg11ki MEFs.

Now they went to AP5Z1, the second binding partner of SPG11, which is reduced in its abundance upon overexpression of Spg11-GFP. I would expect to do the respective control experiment to show that in the absence of SPG11 or in the knock-in cells the amount of AP5Z1 has to increase. However, in the studies by the Huebner group by deletion of Spg11 or the other binding partner Spg15, no increase of AP5Z1 protein levels has been observed. The authors have to comment on this discrepancy.

*Authors response : We agree that this is an important point to discuss, and we failed to do it in our first version. *

*The complete knockout of spatacsin strongly modifies the levels of its partners. We previously showed that spastizin levels are decreased by >90% in Spg11 knockout (Branchu 2017). Furthermore, the levels of AP5Z1 have been shown to be decreased by ~50% in fibroblasts of SPG11 and SPG15 patients (Hirst et al, 2015). *

Our work shows that spatacsin promotes the degradation of AP5Z1 by lysosomes. It is possible that other degradation mechanism may exist, and could explain the lower levels of AP5Z1 in knockout cells. Furthermore, it was proposed that AP5Z1 stability may depend on the presence of spatacsin and spastizin (Hirst et al., 2013)*. Therefore spatacsin may contribute to tightly regulate AP5Z1 levels by contributing both to its stability, and to its degradation. We have carefully discussed this point (p.16). Furthermore, the experiments requested by reviewer 2 in point (vi) that we are planning to perform will help clarify the mechanisms of AP5Z1 degradation both in presence and absence of spatacsin. *

Then the authors found that the selected interaction partner of the exon 32-34 sequence, UBR4, does not bind to the Spg11-GFP construct lacking the domain encoded by exons 32-34 but to the C-terminal domain of Spg11-GFP. Unfortunately, all these IP-experiments were shown as cut and paste figures, preventing the direct comparison between the input and the IP protein amounts (since the information is missing what percentage of the input and the IP has been loaded per lane, the evaluation and significance of these Co-IPs are unclear).

Authors response : We have added in the Figure legend the fact that the input represents 5% of lysate added to the immunoprecipitation assays

v) p9: AP5 (Z1) is a cytoplasmic protein and can be localized on the cytoplasmic surface of lysosomes. How should the GFP-mcherry-AP5Z1 protein enter the lumen of lysosomes justifying the quenching of the GFP signal? A positive control has to be included in the experiment shown in Fig. 4E demonstrating the effect of MG132 under identical conditions of a protein substrate for proteasomal degradation.

Authors response :* We agree this is an important control. We plan to add a control showing accumulation of ubiquitin in lysates upon MG132 treatment to show it was indeed effective. *

vi) Fig. 5A: In contrast to GFP-mcherry-AP5Z1, spastizin-GFP is localized at the cytoplasmic surface of lysosomes (co-staining with LAMP1-mcherry) in wild-type MEFs. In regard to the incomplete data commented under "minor points Fig.4/Suppl.Fig.4", I suggest to perform a simple control experiment with overexpressed GFP-spastizin and mCherry-AP5Z1 in wild-type MEFs (at the best also in Spg11 KO MEF) with and without bafA treatment, which will clearly demonstrate whether single components of the trimeric Spg11, spastizin-AP5Z1 complex are degraded independently of each other in lysosomes.

*Authors response : As stated above, we will perform this control experiment, and will add the data in Figure 5 in future revision. This will help clarify the mechanism of degradation of AP5Z1 and spastizin both in presence and absence of spatacsin. Discussion of this point will also help to clarify the point iv raised by reviewer #2. *

vii) why did the authors neither mention nor discuss the described role of SPG11 in autophago-lysosome reformation (ALR)?

*Authors response : We did not discuss ALR in our first version as we did not investigate autophagic conditions. However, due to the well-described role of spatacsin in ALR, we agree that we should discuss ALR in our manuscript, and we added a paragraph (p.15). *

Minor points

• Figure 1 A, B, D, and G: ER-lysosome contact sites. The quantification of the co-localization of spatacsin-V5 with the ER marker protein GFP-Sec61b has to be given.

Authors response :* We plan to add quantification data performed on STED images showing localization of Spatacsin-GFP together with ER and lysosomal markers. This data will be added in Figure 1. *

Moreover, the authors analyzed overexpressed tagged-proteins only. The results should be compared with the endogenous proteins.

Authors response :* As stated above, there are no good antibodies to endogenous spatacsin for immunostaining. We will add new STED images with antibodies against endogenous Reep5 and Lamp1 to label the ER and lysosomes together with overexpressed spatacsin. Regarding endogenous spatacsin, we could only investigate its localization by subcellular fractionation and western blots comparing wild-type and Spg11 knockout samples. We added biochemical data suggesting that spatacsin is enriched either in the ER or in lysosome membrane associated with the ER. These data have been added in Figure 1 and in text (p.5) and we added a paragraph in discussion regarding spatacsin subcellular localization (p.15). *

p8/Figure 3: what does the 'analysis of trained neural networks' mean?

Authors response : We did not analyzed the trained neural network, but we used this trained neural network to perform image analysis. We clarified the text (p.10).

Figure 4: what happens with the other AP5 subunits?

Authors response : This is a very interesting question. We will test whether overexpression of spatacsin-GFP induces a degradation of some other AP5 subunit, provided we get specific antibody. We will add the data in Figure 4A.

Fig.4F/Suppl.Fig4: live images of GFP-mcherry-AP5Z1 + lysotracker staining have to be shown both for wild-type MEFs with and without bafilomycin A treatment(as in Fig.4F), and in Spg11 KO and Ki MEFs +/- bafA.

Authors response : We will add these data in Figure 4 (WT Mefs +/- Baf A) and in Supplementary Figure 5 (Spg11KO and SPG11D32-34 Mefs +/- Baf).

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

This manuscript highlights an interesting localization of spatacsin in the endoplasmic reticulum (ER)-lysosomes contact sites. In addition, it implicates spatacsin in regulating tubular dynamic lysosomes. Mechanistically, the authors propose that spatacsin interacts with UBR4 to promote the autophagic degradation of its binding partner AP5Z1 at the lysosomes. In turn, this would also regulate the amount of spastizin at the lysosomes, which is known to interact with anterograde motors. The authors further show that AP5Z1 interacts with p150Glued. Thus, the balance between AP5Z1 and spastizin at the lysosomes would determine lysosomal trafficking directionality.

Major Comments

1. Several crucial results of the manuscript are based on quantifications performed on immunofluorescence stainings. Data points in graphs show individual cells or individual lysosomes and the authors apply statistical tests on replicates that cannot be considered biologically independent, since they come from the same experiment or even the same cell. It is recommended to show superplots where both the individual data and the average of each independent experiment is indicated as recommended by Lord et al. (J Cell Biol 2020 219 (6): e202001064.). Statistics should be performed only on independent biological replicates.

Authors response : We agree with the comments of the reviewer regarding data presentation. We have therefore changed the presentation of all graphs of the manuscript using superplots that allow us to show all the points that were analyzed as well as the mean value for each biological replicate, and performed statistical analyses by comparing the biological replicates as proposed in Lord et al, JCB 2020 (10.1083/jcb.202001064).

The authors have used yeast two-hybrid to search for spatacsin interactors. Although in the manuscript they refer to supplementary tables that should show these interactors, the available Tables are confusing and refer to the following downregulation experiments.

Author response : We have added two supplementary data tables (Now Supplementary Tables 1 and 2) to give the list of interactors of wild-type C-terminal domain of spatacsin and spatacsinD32-34, respectively.

Supplementary Tables 3 and 4 now refer to the analysis of the downregulation experiments by respectively the neural network method and the tubular lysosome detection method.

An experiment to demonstrate that endogenous UBR4 and spatacsin interact by co-immunoprecipitation would be crucial.

Authors response : We agree with the reviewer that it would be important to test whether endogenous spatacsin and UBR4 are interacting by co-immunoprecipitation. So far we have not managed to immunoprecipitate either endogenous spatacsin or endogenous UBR4 with the antibodies we tested, which prevents us to test the interactions of endogenous proteins by co-immunoprecipitation. We are not sure we can provide this result.

Several important experiments to unravel the mechanistic role of spatacsin (Figure 4 and 5) are performed upon overexpression. This is a major limitation of the study and the authors should address it as much as possible. Western blots and immunoprecipitations are shown that appear to have been performed only once and have no quantification. As an example, in Fig 4A the difference in levels of AP5Z1 upon spatacsin overexpression or UBR4 downregulation are very minor. I would be very careful in drawing big conclusions, without additional repetitions and additional experiments in an endogenous setting.

*Authors response : We agree that a lot of our experiments used overexpression. We have now added to the manuscript new data obtained in MEFs where we downregulated spastizin or AP5Z1 (Figure 6). They confirm the role of spastizin in the regulation of lysosome dynamics. Furthermore, our new data show that levels of AP5Z1 must be tightly regulated as both overexpression and downregulation of AP5Z1 affects lysosome dynamics (p.12). We also discussed these data carefully (p.16 ). *

Furthermore, we agree that our presentation did not indicate that the western blots were repeated several times. We have now added quantifications for the western blots presented in Figures 4 and 5. Furthermore, we have also added the data showing that downregulation of UBR4 led to higher levels of AP5Z1 in control fibroblasts (Figure 4C).

The authors suggest a model by which UBR4 recruited by spatacsin is involved in autophagic degradation of AP5Z1. The data shown do not support this conclusion. First, in Figure 4A downregulation of UBR4 does not increase levels of AP5Z1 above the control in lane 1, but only when spatacsin is overexpressed. The effect of downregulation of UBR4 in wilt-type cells on AP5Z1 should be investigated. Secondly, there is no experiment directly proving that the stability of AP5Z1 depends on UBR4.

Authors response : We have added new western blots (and quantification) in Figure 4C showing that downregulation of UBR4 increased levels of AP5Z1 in control conditions. The fact that downregulation of UBR4 increased levels of AP5Z1 in control conditions suggests that UBR4 contributes to regulating the levels of AP5Z1. However, we do not show whether UBR4 directly promotes the degradation of UBR4, which has been added in the discussion (p15). To test whether UBR4 affects the stability of AP5Z1, we will monitor whether downregulation of UBR4 by siRNA increases the half-life of AP5Z1. These data will be added on Figure 4.

The authors suggest that the interaction of spatacsin with spastizin or AP5Z1 are in competition. This is an interesting hypothesis, however to conclusively demonstrate this, pull-down experiments in KO cells and not upon extreme overexpression should be performed.

Authors response : We agree that testing the interaction of spatacsin with its partners in SPG15 KO or AP5Z1 KO fibroblasts would be a very good control of our hypothesis. However, we previously showed that the levels of AP5Z1 are lower in SPG15 KO than in control fibroblasts (Hirst et al, 2015), which introduces a bias in the analysis. We therefore plan to concentrate on AP5Z1 fibroblasts and investigate whether interaction of spatacsin with spastizin is modified in these cells. An alternative would be to monitor the effect of siRNA downregulating AP5Z1 on the interaction between spatacsin and spastizin. We will add these data in Figure 5.

Minor comments

1. In figure 1G and 1H the overlapping area between lysosomes and ER is quantified. Considering that the ER occupies a large portion of the field a 90{degree sign} flipped control for both WT and KO would be important to sort out random colocalization. In this direction, it would be also essential to show that the total amount of lysosomes is not different in WT and KO, especially because in figure 1A the lysosomes in WT and KO seem to be different not just in shape but also in number and size. A different number or size of lysosomes affects this analysis.

Authors response :* We added quantifications in Supplementary Figure 1F showing that 90° flipped controls are indeed not capturing the same proportion of contacts between the ER and lysosomes. We also added quantifications in Supplementary Figure 1D-E showing that the average size of lysosomes and the number of lysosomes per unit area are similar in control and Spg11 KO fibroblasts and mentioned it in the text (p.6). If the lysosomal staining appears different in Spg11 KO fibroblasts it is because lysosomes are clustered around the nucleus, an observation that we reported previously (Boutry et al, 2019). *

In the second chapter of the Results, the authors state: "we observed by live imaging a higher number of lysosomes with tubular shape in Spg11+/+ compared to Spg11-/- cells", however the number of elongated lysosomes is quantified per area. Why the number of elongated lysosomes is not quantified over the total amount of lysosomes?

Authors response : The point raised by the reviewer is a fair point. The purpose of our analysis was to compare the number of lysosomes with tubular shape in control and Spg11 KO cells. As the number of lysosomes per unit area is invariant between control and Spg11 KO cells as shown in new data included in Supplementary Figure 1D, normalization to total number of lysosomes or to cell surface reflects the same difference in phenotype.

The In the fourth chapter of the Results, the authors state:" In wild-type MEFs, mCherry was colocalized with lysosomes. In contrast, GFP that is sensitive to pH was poorly colocalized with lysosomes, suggesting that AP5Z1 was mainly inside the acidic subcellular compartment (Figure 4F)." If the aim of the authors is to shown that AP5Z1 is mainly into the lysosome, the amount AP5Z1-mcherry inside and outside the lysosome need to be compared, with a proper statistical analysis. There is also a lot of GFP signal in the cytosol. Why is that?

*Authors response : We agree with the reviewer, we will add quantification of the proportion of AP5Z1-mCherry inside lysosomes on Supplementary Figure 5. *

Regarding the GFP-AP5Z1 signal in the cytosol, AP5Z1 has no transmembrane domain and may thus exist as a cytosolic protein. Since GFP is quenched in the acidic environment of lysosomes, the GFP fluorescence of the mCherry-GFP-AP5Z1 protein is outside lysosomes, and it appears partly cytosolic. Of note, there is also some cytosolic mCherry signal that is less visible due to the high level of mCherry fluorescence in lysosomes. We will clarify this point with the quantification of the proportion of mCherry signal compared to GFP inside the lysosomes and add it in Figure 4.

construct used in the paper is a C-terminal tagged version of spatacsin. The authors should consider to test an N-terminal tagged construct at least for the localization experiments.

Authors response : We added an immunostaining image of Spatacsin with an N-terminal tag (Supplementary Figure 1B) and mentioned it in the text (p.6). As spatacsin with a C-terminal tag, it presents a diffuse distribution that poorly co-localizes with lysosomes.

Figure 5C: a negative control and the quantification are missing.

Authors response : A non-transfected cell is present on Figure 5C, visible thanks to the Lamp1 immunostaining, and that we considered as a negative control. In this non-transfected cell, we detected no PLA signal. We added an asterisk to point the non-transfected cell on Figure 5C. Quantification will also be added in the revised version after we have performed the PLA experiment required by Reviewer 1.

Reviewer #3 (Significance (Required)):

Since spatacsin, AP5Z1 and spastizin are all implicated in hereditary spastic paraplegia, the data are of potential interest not only for basic cell biology, but also to understand the pathogenesis of the disease. In addition, the manuscript proposes a novel model regulating trafficking of dynamic lysosomes.

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

Pierga et al. reveal subtle differences in lysosome morphology, ER-contact, and trafficking in the absence of Spatascin. These data are replicated with a truncated Spatascin, presumably a loss of function. Two-hybrid screening of the deleted sequence from this truncation for interactors and then asked whether these hits could phenocopy the lysosome morphology changes. This led to an assertion for a role for ubiquitination in these effects. Rather than these hits the group then investigates previously known Spatascin interactors and reports similar complex but subtle abnormalities via overexpression or knockdown of these. While data show overlapping phenotypes by modulation Spatascin, AP5z1, and Spastizin, the manuscript is confusing, leaps from experiment to experiment, and does not provide novel rigorous mechanisitic insight. It conflates all the discrete lysosomes aspects into a collective to link them. The title is over-stated and not appropriate for the experiments.

The localization of endogenous Spatascin is lacking - over-expression is prone to artifact and the punctate data on the V5 suggests much more work is needed to understand where in the cell it is. It would seem much more work is needed here.

Authors response : As stated by reviewer 1, there are no good antibody to endogenous spatacsin, and therefore we have to rely on expression of tagged spatacsin to study its localization by immunofluorescence. When performing the images, we avoided the cells with the highest ovexpression of tagged spatacsin. Yet, we agree that this is still overexpression. That’s why we included subcellular fractionation data where we can detect endogenous spatacsin (Figure 1A-1B). These data confirmed that spatacsin is enriched in the ER or in lysosome fraction tightly associated with the ER.

Furthermore, the EM data (1E) would suggest the far majority of lysosomes are in contact with ER - these seems uncharacteristic.

Authors response : The EM data in figure 1E indeed shows that the majority of lysosomes are in contact with the ER, as previously shown by other groups (Friedman et al, 2013, Höglinger et al, 2019).

The phenotypes analyzed are very subtle, and while statistically significant the biological impact is unclear - in many cases individual lysosomes (or lysosome-ER contacts) are considered as an 'n'. While these results are probed across multiple independent experiments the batch effects and how uniform per cell the events are is unclear.

Authors response : We agree with the comments of the reviewer regarding data presentation. ‘n’ represented individual cells, but did not actually take into account the variability across experiments. We have therefore changed the presentation of all graphs of the manuscript using superplots that allow us to show all the points that were analyzed as well as the mean value for each biological replicate, and performed statistical analyses by comparing the biological replicates as proposed in Lord et al, JCB 2020 (10.1083/jcb.202001064).

In fig 2H critical data are missing - the effect of Spatascin KO on the transition between these morphologies should be considered as in G. Otherwise the relevance is unclear.

Authors response : We have added this quantification on Figure 2I. It shows that transition of morphology of lysosomes from round to tubular in Spg11 KO cells is still associated with a change of speed, although the average speed attained is halved compared to conditions where spatacsin is present. This shows that loss of spatacsin does not abolish morphological transition of lysosomes but limit their speed in the tubular shape. We commented on this new data in the text (p.8).

The impact of over-expressing a lysine-null Ub ( Fig 3) is far too crude and non-specific to have meaning here. It is assumed that the only proteins affected are those of interest. This is consistent with much of the paper where "true-true-and unrelated" is more likely than the presumption of causality.

Authors response : It is true that the expression of lysine-null ubiquitin is really crude and may impact many different cellular pathways. Furthermore, the results obtained with the lysine-null ubiquitin do not contribute to the rest of the paper. We therefore removed the original Fig3G, H, I and Fig 4B and updated the text accordingly (p.10).

The blots in Fig4 are a relatively poor quality and not quantified over repetition.

*Authors response :Spatacsin and spastizin are large proteins, and there is not much choice for antibodies able to detect these proteins. Yet we have validated their specificity by western blot using knockout cells (spatacsin) (Supplementary Figure 4 A-B) or siRNA (spastizin) (Supplementary Figure 7B). We agree that our presentation did not indicate that the western blots were repeated several times. We have added quantifications for the western blots present in Figures 4 and 5. We also changed some illustrative western blots to improve quality. *

Controls are missing and Fig5 suffers from a reliance on over-expression - there is a massive over-expression of AP5Z1 which may be affected the stoichiometry of these overall interactions, but with an n=1 its hard to know and its not clear what these data add. Again, while statistically significant (5E and F) due to the nature of data analysis (every lysosome=n of 1) it is not clear how biologically significant UBR4 siRNA or AP5Z1 over-expression is - as the accumulation of AP5Z1 in these two conditions is orders of magnitude apart - again likely unrelated.

Authors response : We added quantification for this western blot (Supplementary Figure 6A).

*As stated above we have changed the representation of the graphs. Each point represents one cell, and we included the mean value for each biological replicate. *

Preventing degradation of AP5Z1 by UBR4 siRNA or overexpression of AP5Z1 do not indeed have the same effect on total AP5Z1 but do have a similar effect on the interaction of spatacsin with its partners evaluated by co-immunoprecipitation, as illustrated by the quantifications that we have added. We clarified this in the text (p.12). As requested by reviewer 3, we will also investigate the effect of AP5Z1 knockout or downregulation on the interaction between spatacsin and spastizin assessed by co-immunoprecipitation. These data will be added in Figure 5 and will strengthen our conclusions.

Fig 6 begins to conflate the fact that different lysosome morphologies appear to have different trafficking properties even in WT cells and that many of these targets affect morphology - therefore to conclude a direct effect on trafficking seems inappropriate.

Authors response : In original Figure 6, we showed that Kif13A-ST and p150CC1 changed the proportion of tubular lysosomes (previous Figure 6 and H), and the data showing that these constructs changed the trafficking of lysosomes were presented in Supplementary Figure 5 B-C. We have now moved the data showing the effect of Kif13A-ST and p150CC1 in the main Figure (Figure 6F and 6I) to facilitate the interpretation of the data. Therefore, expression of Kif13A-ST and p150CC1 do not only affect the morphology of lysosomes, but also impaired their trafficking. We thus do not extrapolate lysosome dynamics from their morphology, we actually quantify lysosome dynamics.

Fig 7 extends this into polar cells (neurons) but still it is not clear whether form (morphology) dictates function (likelihood of trafficking or directionality.

Authors response : We did not only analyzed neurons because they are polarized cells, but because neurons are the main cells affected by neurodegeneration observed in absence of spatacsin (Branchu et al, 2017). We added new data on Figure 7 showing that tubular lysosomes in axons are actually more dynamic than round lysosomes, as observed in fibroblasts. We added these data in Figure 7 and text (p.13).

Investigation of lysosome trafficking in axons also allowed us to investigate the directionality of movement, which is difficult in MEFs. We clarified this point in the text (p.13).

In sum, there is a lot of data that collectively points to a partial localization of Spatascin at Er-lysosome contacts and an influence on morphology and trafficking of lysosomes in the cell, but at the end of the day very new mechanism is brought to light.

Authors response : The mechanisms regulating trafficking of lysosomes are far from being fully resolved. Our manuscript shows that spatacsin contributes to this regulation by modulating the degradation of AP5Z1. This in turn regulate the lysosomal association of AP5Z1 and spastizin that interact with motor proteins to control lysosomal dynamics.

Reviewer #4 (Significance (Required)):

This manuscript is directed to the basic cell biology community - involving ER, lysosome, and microtubule dependent trafficking. There are some new analytical tools employed and many co-factors and binding partners of Spatascin considered but frankly too many to adequately and rigorously control for. Because of this the manuscript is very unfocused, hard to follow and makes too many assumptions about shared dynamics ? necessarily arising from shared morphology - lysosomes are highly dynamic and can be affected by virtually any change in intracellular trafficking or protein/membrane transport. This is not appropriately considered.

Authors response : We have clarified our manuscript to show that dynamics is not necessarily arising from a tubular morphology. It turns out that lysosomes with a tubular morphology indeed are more dynamic that lysosomes with a round morphology. Importantly, in all our experiments dealing with lysosomal dynamics, we have actually included a quantification of lysosome dynamics using time lapse imaging as detailed in methods (p.21).

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Referee #4

Evidence, reproducibility and clarity

Pierga et al. reveal subtle differences in lysosome morphology, ER-contact, and trafficking in the absence of Spatascin. These data are replicated with a truncated Spatascin, presumably a loss of function. Two-hybrid screening of the deleted sequence from this truncation for interactors and then asked whether these hits could phenocopy the lysosome morphology changes. This led to an assertion for a role for ubiquitination in these effects. Rather than these hits the group then investigates previously known Spatascin interactors and reports similar complex but subtle abnormalities via overexpression or knockdown of these. While data show overlapping phenotypes by modulation Spatascin, AP5z1, and Spastizin, the manuscript is confusing, leaps from experiment to experiment, and does not provide novel rigorous mechanisitic insight. It conflates all the discrete lysosomes aspects into a collective to link them. The title is over-stated and not appropriate for the experiments.

The localization of endogenous Spatascin is lacking - over-expression is prone to artifact and the punctate data on the V5 suggests much more work is needed to understand where in the cell it is. It would seem much more work is needed here. Furthermore, the EM data (1E) would suggest the far majority of lysosomes are in contact with ER - these seems uncharacteristic.

The phenotypes analyzed are very subtle, and while statistically significant the biological impact is unclear - in many cases individual lysosomes (or lysosome-ER contacts) are considered as an 'n'. While these results are probed across multiple independent experiments the batch effects and how uniform per cell the events are is unclear.

In fig 2H critical data are missing - the effect of Spatascin KO on the transition between these morphologies should be considered as in G. Otherwise the relevance is unclear.

The impact of over-expressing a lysine-null Ub ( Fig 3) is far too crude and non-specific to have meaning here. It is assumed that the only proteins affected are those of interest. This is consistent with much of the paper where "true-true-and unrelated" is more likely than the presumption of causality.

The blots in Fig4 are a relatively poor quality and not quantified over repetition.

Controls are missing and Fig5 suffers from a reliance on over-expression - there is a massive over-expression of AP5Z1 which may be affected the stoichiometry of these overall interactions, but with an n=1 its hard to know and its not clear what these data add. Again, while statistically significant (5E and F) due to the nature of data analysis (every lysosome=n of 1) it is not clear how biologically significant UBR4 siRNA or AP5Z1 over-expression is - as the accumulation of AP5Z1 in these two conditions is orders of magnitude apart - again likely unrelated.

Fig 6 begins to conflate the fact that different lysosome morphologies appear to have different trafficking properties even in WT cells and that man of these targets affect morphology - therefore to conclude a direct effect on trafficking seems inappropriate. Fig 7 extends this into polar cells (neurons) but still it is not clear whether form (morphology) dictates function (likelihood of trafficking or directionality.

In sum, there is a lot of data that collectively points to a partial localization of Spatascin at Er-lysosome contacts and an influence on morphology and trafficking of lysosomes in the cell, but at the end of the day very new mechanism is brought to light.

Significance

This manuscript is directed to the basic cell biology community - involving ER, lysosome, and microtubule dependent trafficking. There are some new analytical tools employed and many co-factors and binding partners of Spatascin considered but frankly too many to adequately and rigorously control for. Because of this the manuscript is very unfocused, hard to follow and makes too many assumptions about shared morphology necessarily arising from shared morphology - lysosomes are highly dynamic and can be affected by virtually any change in intracellular trafficking or protein/membrane transport. This is not appropriately considered.

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Referee #3

Evidence, reproducibility and clarity

This manuscript highlights an interesting localization of spatacsin in the endoplasmic reticulum (ER)-lysosomes contact sites. In addition, it implicates spatacsin in regulating tubular dynamic lysosomes. Mechanistically, the authors propose that spatacsin interacts with UBR4 to promote the autophagic degradation of its binding partner AP5Z1 at the lysosomes. In turn, this would also regulate the amount of spastizin at the lysosomes, which is known to interact with anterograde motors. The authors further show that AP5Z1 interacts with p150Glued. Thus, the balance between AP5Z1 and spastizin at the lysosomes would determine lysosomal trafficking directionality.

Major Comments

1. Several crucial results of the manuscript are based on quantifications performed on immunofluorescence stainings. Data points in graphs show individual cells or individual lysosomes and the authors apply statistical tests on replicates that cannot be considered biologically independent, since they come from the same experiment or even the same cell. It is recommended to show superplots where both the individual data and the average of each independent experiment is indicated as recommended by Lord et al. (J Cell Biol 2020 219 (6): e202001064.). Statistics should be performed only on independent biological replicates.
2. The authors have used yeast two-hybrid to search for spatacsin interactors. Although in the manuscript they refer to supplementary tables that should show these interactors, the available Tables are confusing and refer to the following downregulation experiments. An experiment to demonstrate that endogenous UBR4 and spatacsin interact by co-immunoprecipitation would be crucial.
3. Several important experiments to unravel the mechanistic role of spatacsin (Figure 4 and 5) are performed upon overexpression. This is a major limitation of the study and the authors should address it as much as possible. Western blots and immunoprecipitations are shown that appear to have been performed only once and have no quantification. As an example, in Fig 4A the difference in levels of AP5Z1 upon spatacsin overexpression or UBR4 downregulation are very minor. I would be very careful in drawing big conclusions, without additional repetitions and additional experiments in an endogenous setting.
4. The authors suggest a model by which UBR4 recruited by spatacsin is involved in autophagic degradation of AP5Z1. The data shown do not support this conclusion. First, in Figure 4A downregulation of UBR4 does not increase levels of AP5Z1 above the control in lane 1, but only when spatacsin is overexpressed. The effect of downregulation of UBR4 in wilt-type cells on AP5Z1 should be investigated. Secondly, there is no experiment directly proving that the stability of AP5Z1 depends on UBR4.
5. The authors suggest that the interaction of spatacsin with spastizin or AP5Z1 are in competition. This is an interesting hypothesis, however to conclusively demonstrate this, pull-down experiments in KO cells and not upon extreme overexpression should be performed.

Minor comments

1. In figure 1G and 1H the overlapping area between lysosomes and ER is quantified. Considering that the ER occupies a large portion of the field a 90{degree sign} flipped control for both WT and KO would be important to sort out random colocalization. In this direction, it would be also essential to show that the total amount of lysosomes is not different in WT and KO, especially because in figure 1A the lysosomes in WT and KO seem to be different not just in shape but also in number and size. A different number or size of lysosomes affects this analysis.
2. In the second chapter of the Results, the authors state: "we observed by live imaging a higher number of lysosomes with tubular shape in Spg11+/+ compared to Spg11-/- cells", however the number of elongated lysosomes is quantified per area. Why the number of elongated lysosomes is not quantified over the total amount of lysosomes?
3. The In the fourth chapter of the Results, the authors state:" In wild-type MEFs, mCherry was colocalized with lysosomes. In contrast, GFP that is sensitive to pH was poorly colocalized with lysosomes, suggesting that AP5Z1 was mainly inside the acidic subcellular compartment (Figure 4F)." If the aim of the authors is to shown that AP5Z1 is mainly into the lysosome, the amount AP5Z1-mcherry inside and outside the lysosome need to be compared, with a proper statistical analysis. There is also a lot of GFP signal in the cytosol. Why is that?
4. construct used in the paper is a C-terminal tagged version of spatacsin. The authors should consider to test an N-terminal tagged construct at least for the localization experiments.
5. Figure 5C: a negative control and the quantification are missing.

Significance

Since spatacsin, AP5Z1 and spastizin are all implicated in hereditary spastic paraplegia, the data are of potential interest not only for basic cell biology, but also to understand the pathogenesis of the disease. In addition, the manuscript proposes a novel model regulating trafficking of dynamic lysosomes.

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Referee #2

Evidence, reproducibility and clarity

In this study Pierga et al. report that SPG11 (spatacsin) is an ER-resident protein involved in the regulation of ER-lysosome contact sites (in particular tubular lysosomes) and subsequent faster motility of tubular lysosomes, as well in the degradation of AP5Z1 (SPG48), which forms a heterotrimeric complex with SPG15 (spastizin) and SPG11. This complex has been localized by several groups on the cytoplasmic side of LAMP-1-positive lysosomes. In addition, mutations in SPG11, SPG15, and SPG48 patients share various clinical features and were supported by biochemical/cell biological data from Spg11 and Spg15 KO mouse models and cultured cells both from patients and mice, respectively, demonstrating e.g. accumulation of autolysosome storage material, defects in the autophagic lysosome reformation process, and the loss of cortical motoneurons and Purkinje cells.

Major concerns:

1. Fig. 1, 2, 3: major disadvantage of this study is the analysis of overexpressed proteins (SPG11-V5, GFP-Sec61,and Lamp1-mCherry) which might contribute to the observed strong expression of SPG11-V5 in the ER/ER-enriched fraction. The results should be compared with the endogenous expressed proteins. In Fig. 1C the lack of the mature Cathepsin D form which is proteolytically generated only in lysosomes from the higher molecular mass precursor is misleading and should be related to presence of lysosomal membrane proteins. Fig. 1D: the TEM image shows only a single lysosome and proposed ER contact zones in wt-MEFs without comparison with Spg11 KO MEFs (only in the quantification). Without double immunogold labeling of SPG11 (and their lack on SPG11 KO cell lysosomes) and known ER contact-site proteins this image and the conclusion are insufficient.
2. The rationale for the selection of the deleted Spg11 region 32-34 is not clear. What are the symptoms of this Spg11 knock-in mouse? A more detailed description of the phenotype is required! Is the phenotype including the accumulation of LC3-positive material similar to the phenotype of the SPG11 KO mouse which has been published by Varga et al.(2015) and Branchu et al. (2017) ? If not, is the new mechanisms reported here not so important?
3. p8/Fig. 3F/Suppl.Fig.3F- the most important part of the manuscript: what are the parameters of lysosomal staining in images that were used to identify genes important for lysosome tubulation by the neural network? I cannot understand how the authors predict the probability of the cell to be considered as an Spg11 KO fibroblast (why not as an Spg11 32-34 knock-in fibroblast?) as the basis for the selection of interaction candidates. A simple statement that the neural network approach identified those genes is too weak and requires more convincing experimental data. It has to be shown at least for the 8 positive genes in both approaches how the siRNA treatments of these genes phenocopied the lysosomal changes and of course the effect of the downregulation on the protein level of their products both in wild-type control and Spg11 32-34 knock-in MEF. The Suppl. Fig.3F is completely unclear. How were the Y2H interaction partner validated? Did the authors use the identified 8 interaction candidates as full length bait to demonstrate the interaction with the Spg11 exons 32-34 ? p8/Fig.3F: the genes identified in both approaches have to be listed in the Fig. 3F-Table. The GO process- ubiquitin-dependent protein catabolic process is neither positive for the neural network nor for the directed analysis but positive for both analyses? Please explain. Similarly, the GO process proteolysis involved in cellular protein catabolic process -is not positive for the neural network analysis but again positive for both analyses. For Fig. 3G the mutant ubiquitin-K0 staining in wild-type MEF cells has to be shown as well as for the Spg11 ki/KO MEFs (+ quantification of the respective data)
4. The interpretation of the Y2H-interactome analysis by the authors is hard to follow. They searched with the exon 32-34 cDNA for binding partner, selected 3 degradative GO processes and showed by overexpression of a mutant Ub-K0 plasmid in wild-type MEFs a decreased number of tubular lysosomes, as well as their dynamics (without showing the control data in Spg11 KO or ki-MEFs). Thus, poly-ub of proteins should be in some way responsible for a lysosomal phenotype of Spg11ki MEFs. Now they went to AP5Z1, the second binding partner of SPG11, which is reduced in its abundance upon overexpression of Spg11-GFP. I would expect to do the respective control experiment to show that in the absence of SPG11 or in the knock-in cells the amount of AP5Z1 has to increase. However, in the studies by the Huebner group by deletion of Spg11 or the other binding partner Spg15, no increase of AP5Z1 protein levels has been observed. The authors have to comment on this discrepancy. Then the authors found that the selected interaction partner of the exon 32-34 sequence, UBR4, does not bind to the Spg11-GFP construct lacking the domain encoded by exons 32-34 but to the C-terminal domain of Spg11-GFP. Unfortunately, all these IP-experiments were shown as cut and paste figures, preventing the direct comparison between the input and the IP protein amounts (since the information is missing what percentage of the input and the IP has been loaded per lane, the evaluation and significance of these Co-IPs are unclear).
5. p9: AP5 (Z1) is a cytoplasmic protein and can be localized on the cytoplasmic surface of lysosomes. How should the GFP-mcherry-AP5Z1 protein enter the lumen of lysosomes justifying the quenching of the GFP signal? A positive control has to be included in the experiment shown in Fig. 4E demonstrating the effect of MG132 under identical conditions of a protein substrate for proteasomal degradation.
6. Fig. 5A: In contrast to GFP-mcherry-AP5Z1, spastizin-GFP is localized at the cytoplasmic surface of lysosomes (co-staining with LAMP1-mcherry) in wild-type MEFs. In regard to the incomplete data commented under "minor points Fig.4/Suppl.Fig.4", I suggest to perform a simple control experiment with overexpressed GFP-spastizin and mCherry-AP5Z1 in wild-type MEFs (at the best also in Spg11 KO MEF) with and without bafA treatment, which will clearly demonstrate whether single components of the trimeric Spg11, spastizin-AP5Z1 complex are degraded independently of each other in lysosomes.
7. why did the authors neither mention nor discuss the described role of SPG11 in autophago-lysosome reformation (ALR)?

Minor points

• Figure 1 A, B, D, and G: ER-lysosome contact sites. The quantification of the co-localization of spatacsin-V5 with the ER marker protein GFP-Sec61b has to be given. Moreover, the authors analyzed overexpressed tagged-proteins only. The results should be compared with the endogenous proteins.
• p8/Figure 3: what does the 'analysis of trained neural networks' mean?
• Figure 4: what happens with the other AP5 subunits?
• Fig.4F/Suppl.Fig4: live images of GFP-mcherry-AP5Z1 + lysotracker staining have to be shown both for wild-type MEFs with and without bafilomycin A treatment(as in Fig.4F), and in Spg11 KO and Ki MEFs +/- bafA.

Significance

see above.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This paper identifies a role for the hereditary spastic paraplegia protein spatacsin in lysosome morphology, positioning and dynamics, and undertakes detailed mechanistic studies to try to identify the mechanism for this effect. In doing so the paper elucidates further mechanistic information about the properties of two other hereditary spastic paraplegia proteins, spastizin and AP5Z1. The work is done in mammalian cells and uses a combination of over-expression, depletion and biochemical studies. The main findings are:

1. The authors present evidence that spatacsin is an ER-localised protein.
2. Murine embryonic fibroblasts lacking spatacsin have a reduced number of tubular lysosomes and the remaining lysosomes are less motile. In general, a relationship between tubular lysosome morphology and lysosome motility, often in association with the endoplasmic reticulum (ER), is demonstrated. These tubular lysosomes are catalytically active and acidic.
3. In terms of mechanism of this effect, by combining a yeast-two hybrid and siRNA phenotypic screen, the authors identify a number of spatacsin-interacting proteins that also regulate lysosomal tubulation. The most important of these for the purposes of this paper is UBR4, an E3 ubiquitin ligase.
4. The authors show that spatacsin and UBR4 promote degradation of AP5Z1, and that this property required the ability of spatacsin to interact with UBR4. Somewhat surprisingly, as AP5Z1 is a coat protein, this degradation appeared to occur within the lumen of the lysosome - the authors speculate how this could be in the discussion.
5. The authors then demonstrate that AP5Z1 and spastizin, both hereditary spastic paraplegia proteins, compete for binding with spatacsin.
6. The relationship between spatacsin, spastizin, AP5Z1 and motor proteins in then examined. There is a known interaction between spastizin and KIF13A and expression of a dominant negative KIF13A protein reduced lysosomal tubulation. The authors then demonstrate an interaction between AP5Z1 and the p150Glued dynein/dynactin complex member, then showed that expression of a dominant negative p150Glued protein reduced lysosomal tubulation.
7. Finally, that authors demonstrate the relevance of these findings to neurons, the target cells of hereditary spastic paraplegia, by showing that lysosomal tubulation and axonal transport are reduced in mouse neurons lacking spastacsin, and that depletion of UBR4 or AP5Z1 affected these as expected from the experiments above.

Major comments:

Overall I believe that the key conclusions of this paper are generally convincing and that the work is of high quality. However, I do have some reservations:

1. The localisation of spatacsin on the ER. It is always difficult to be convinced about colocalization of a diffuse punctate marker and the ER. From the STED experiments in figure 1, while it definitely seems that there is some spatacsin on the ER, there also appears to be some spatacsin puncta that are not. I'd like to know if these puncta represent lysosome-associated spatacsin. This is important for interpretation of the subsequent experiments (see point 3 below). I also think quantification of these co-localisation will increase confidence in the results. In addition, a caveat of the immunofluorescence studies is that they use over-expressed spatacsin. I appreciate that there are no good antibodies to endogenous spatacsin, but I don't think this limitation is sufficiently acknowledged. As the claim of ER-localisation is critical for the proposed mechanistic model, and in the absence of experiments with endogenously tagged spatacsin, this makes the biochemical fractionation studies of figure 1C very important. To make these more convincing I would prefer to see additional control markers to verify the separation of lysosomal and ER compartments - e.g. lamp1, lamp2, an ER tubular marker such as a REEP5 or a reticulon.
2. The authors generally do a good job of quantifying their results. However, this is lacking for the biochemical experiments (immunoblotting and IP) in figures 4 and 5, and I would prefer to see these quantified (the quantification should include data from repeat experiments so that we can judge the reproducibility of the results).
3. On page 10, referring to the proximity ligation results, the authors comment: "This suggests that the spatacsin-spastizin interaction occurs at contact sites between the ER and lysosomes to allow spastizin recruitment to lysosomes". I'm not sure this statement is fully supported, as mentioned at point 1 above it is possible that some steady state spatacsin is at lysosomes. To fully support this, we'd need to see the PLA signal also convincingly co-localise with an ER marker.
4. In figure 6C and D the effect of spastizin on lysosomal tubulation and dynamics is investigated. Wartmannin treatment is used to do this, as it is known to remove spastizin from lysosomes. However, this is a very indirect manipulation that could have many other consequences and it would be better to demonstrate this directly by showing the effect of depletion of spastizin on lysosomal morphology/dynamics. I also think the role of AP5Z1 in tubulation/dynamics would be better supported with additional experiments to deplete the protein - at present only over-expression is examined.

5. While the experiments showing that over-expression of dominant negative forms of KIF13A and p150Glued affect lysosomal tubulation/dynamics provide good circumstantial evidence that spatacsin influences these lysosomal properties via its interactions with spastizin and AP5Z1 (which bind to these motor proteins), the authors have not shown that the interaction of the motor proteins with spastizin and AP5Z1 is required for this ability to regulate lysosome tubulation/dynamics. This means that the model presented in figure 7 is not fully supported by the data. If the authors have been able to map the binding regions for these interactions then perhaps this could be investigated with rescue experiments, although I appreciate that this is potentially a major piece of work and perhaps outside the scope of this paper. An alternative would be that the authors acknowledged this part of the model as somewhat speculative.

6. Are the data and the methods presented in such a way that they can be reproduced?

Yes - Are the experiments adequately replicated and statistical analysis adequate?

In general I am not convinced that the statistical tests are applied rigorously in this paper. Most experiments are done three times, but the "n" used for statistical testing is typically chosen as, e.g. the number of cells, number of lysosomes, rather than number of biological repeat experiments. This means that inter-experimental variability is not rigorously taken into account. A more rigorous practice would be to use the mean measures for each of three biological repeats and apply the statistical tests to the three means, so n=3 if three repeats were done. Superplots would be a nice way to graphically display these data.

Minor comments:

1. In supplementary figure 3D I cannot honestly say that I see the smaller band.
2. When first called out, I expected supplementary tables 1 and 2 to show the list of interactors with wild-type spatacsin and spatacsind32-34 respectively, but this is not what they show.
3. The experiments in Figure 4A are a little problematic in the way that they are called out. The first call refers to just a small subset of the data in the figure, and the figure is then called out at various points later in the paper. This is quite confusing. Is there any way this could be simplified?
4. The section on page 10: "Spatacsin also interacts with spastizin, and is required to recruit spastizin to lysosomes (Hirst et al., 2021). ........ We hypothesized that spatacsin interaction with spastizin was required for spastizin localization to lysosomes." Is odd, as the authors seem to be hypothesising an observation that they have just said has already been demonstrated.
5. Can the authors explain why there is so little interaction between wild-type KIF13A and spastizin?
6. In figure 6G p150Glued signal is also present in the control IP lane, which casts doubt on the specificity of the interaction. Could the authors generate a cleaner result?

7. I would be interested to see how AP5Z1 expression differs between neurons with and without spatacsin- we would expect similar results to those shown in the MEFS.

8. Are prior studies referenced appropriately?

Yes. - Are the text and figures clear and accurate?

Yes - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Overall I thought the presentation was good. However, this is a complex paper and anything that the authors can do to simplify the textual descriptions of the experiments would be helpful. There are quite a few long multiphrase/multiclause sentences that could perhaps be broken up or simplified, e.g. I had to read the following three or four times to understand it: "Downregulation of UBR4 that prevented degradation of AP5Z1mediated by spatacsin (Figure 4A) led to higher interaction of spatacsin with AP5Z1 and decreased the interaction of spatacsin with spastizin (Figure 4A)."

Referees cross-commenting

Thanks for the opportunity to comment on the other reviews. It does seem that there is a consistent theme that reviewers are concerned about the over-reliance on over-expression experiments and the need for additional experiments using endogenous antibodies or protein depletion methodologies to strengthen the data. In addition, I and at least one other reviewer feel that it is not adequate to use number of cells as the "n" for statistical testing, and that true biological repeats are needed.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

I think this paper represents a significant conceptual advance in our understanding of the mechanisms by which lysosomal dynamics are controlled in non-polarised cells and neurons. In addition, it elucidates mechanisms that may underlie multiple forms of hereditary spastic paraplegia, a hereditary form of motor neuron disease.<br /> - Place the work in the context of the existing literature (provide references, where appropriate).

This is a significant conceptual advance on the current literature on spatacsin and on the molecular mechanisms controlling lysosomal morphology/dynamics. The paper elucidates important mechanistic details of the relationship between three key proteins involved in hereditary spastic paraplegia, while also shedding light on the basic biology of lysosomal morphology and dynamics. - State what audience might be interested in and influenced by the reported findings.

Basic cell biologists interested in the ER, in lysosomes, in ER-organelle contacts. Scientists interested in the causation of hereditary spastic paraplegias. - 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.

Membrane traffic, lysosome function, ER-endosome contacts, hereditary spastic paraplegia.

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Reply to the reviewers

Manuscript number: RC-2022-01683

Corresponding author(s): Prof Andrew Macdonald, Dr Ethan Morgan

1. General Statements [optional]

We are very appreciative of the helpful and insightful comments provided by the reviewers, which will greatly aid in improving this manuscript. We were delighted by the many positive comments we received, highlighting the “high quality” data and praising our “detailed and carefully constructed” experiments, which together reveal an “interesting and novel mechanism” of HPV-driven cervical carcinogenesis.

To summarise our key findings, we identify the host ATP-sensitive potassium ion (KATP) channel as a critical driver of proliferation and HPV oncoprotein expression in HPV+ cervical cancer cells. Use of pharmacological inhibitors and activators of KATP channels revealed that HPV oncoprotein expression correlates with channel activity, findings that were validated via siRNA/shRNA knockdown and overexpression strategies. Indeed, HPV was found to enhance expression of the ABCC8 gene (encoding the SUR1 KATP channel subunit), likely in a manner dependent on the E7 oncoprotein. We also reveal that channel knockdown impeded HPV+ cervical cancer cell proliferation, both in cell culture monolayer and, importantly, in tumour xenograft experiments. This loss of proliferation may be associated with induction of a G1 cell cycle arrest. Finally, we demonstrate that KATP channels are capable of activating ERK1/2 signalling and, in turn, the AP-1 transcription factor, leading to recruitment of AP-1 to the HPV18 promoter. Significantly, this study is the first to our knowledge to explicitly demonstrate modulation of ion channel expression and activity by HPV, and that this can contribute to host cell transformation. We believe the potential for use of the clinically available KATP channel inhibitors as novel therapies for HPV-associated malignancies should therefore be evaluated in future studies.

Outlined below, in a point-by-point manner, are the changes we have already incorporated to improve the precision and clarity of the manuscript, as well as the additional data we intend to add in order to strengthen our findings.

2. Description of the planned revisions

Reviewer #1 (Evidence, reproducibility and clarity (Required)): Addressing the following major points would help to strengthen the impact of the work:

1. The paper would be greatly strengthened by addressing whether knockdown of SUR1 and knockdown of E6/E7 are affecting cell viability. siRNA depletion of E6 and E7 will cause HeLa and SiHa cells to senesce; at what time point post knockdown were the experiments performed? Is it possible to perform CellTiterGlo or other cell viability assays to confirm that the phenotypes observed upon E6/E7 depletion and upon SUR1 depletion or drug treatment are not the result of cell death/senescence/toxicity?

We agree that an assessment of cell viability following the treatments/transfections performed will strengthen the manuscript. We will therefore perform the suggested CellTiterGlo assay using both HeLa and SiHa cells after glibenclamide treatment, SUR1 knockdown, and E6/E7 knockdown.

1. There is a major concern regarding whether SUR1 protein is produced at a biologically relevant level in SiHa and HeLa cells, in which most of the experiments in the paper were conducted. Protein levels are assessed in Fig 2 by immunostaining in raft cultures and in a cervical cancer tissue microarray. However, protein levels are otherwise not examined, especially in SiHa and HeLa cells. Is SUR1 protein produced in these cells? Are its levels reduced by the knockdown approaches? The fold change RNA data presented in figure 2A does not convincingly address this question, since even an 8-fold increase of ABCC8 mRNA over a low background level might not have biological significance. It would be very helpful to measure SUR1 protein in several of the experiments in HeLa and SiHa cells.

We accept the concern of the reviewer regarding the absence of an assessment of SUR1 protein levels in HeLa and SiHa cells. There is a critical lack of high-quality antibody reagents available for the detection of SUR1, a common phenomenon within the ion channel field. We have therefore been unable to reliably detect SUR1 via immunoblot using the antibodies we have tested thus far. Nevertheless, we would argue that our other experiments in these cell lines demonstrate that not only are KATP channels expressed at biologically relevant levels but, more importantly, are active in these cell lines. Patch clamping electrophysiology, the gold-standard technique for assessing ion channel functionality, was performed in HeLa cells and the changes in current observed following inhibitor/activator application suggests that the channels are active, and by extension, that SUR1 protein must be present. Furthermore, DiBAC4(3) assays were performed following inhibitor treatments, channel stimulation, SUR1 knockdown, and HPV E7 knockdown. Although this involves an assessment of plasma membrane polarisation, and therefore is not a direct measurement of KATP channel activity, the changes observed are consistent with our expectations (e.g. increased DiBAC4(3) fluorescence with glibenclamide treatment, indicative of membrane depolarisation, is consistent with a loss of K+ ion efflux via KATP channels). However, we recognise that providing protein expression data in HeLa and SiHa cells would make our conclusions more convincing. We will therefore continue our search for antibody reagents that will allow us to reliably detect SUR1 protein in HPV+ cell lines by western blot. We will also pursue other detection methods in these cell lines, including immunofluorescence and immunohistochemistry. We hope that we are successful in our optimisation, allowing us to validate that SUR1 protein levels are reduced following our knockdown approaches.

1. The authors should address the idea of off-target effects, either experimentally or, more feasibly, by discussing the possibility of non-specific effects of SUR1 knockdown. They use a pool of four siRNAs to SUR1 and the risk of off-target effects would be greatly reduced if individual siRNAs were tested and shown to have the same effect as one another. Similarly, several experiments use just one shRNA, limiting the ability to draw conclusions.

To address off-target effects, we will repeat some of the experiments performed in this manuscript using individual siRNAs. HeLa and SiHa cells will be transfected with each of the four siRNAs individually and the impact on HPV E6 and E7 expression examined by RT-qPCR and western blot. Further, we will also repeat colony formation assays and DiBAC4(3) assays to ensure that each siRNA has a similar effect on proliferation and membrane polarisation respectively.

1. Finally, since many of the experiments rely on knockdown approaches that show similar readouts, a rescue experiment (restore sh or si-resistant SUR1 and assess the impact on the phenotype) would confirm that the effects being observed are due to changes in SUR1 levels and not to off-target effects.

We agree that rescue experiments would greatly strengthen the manuscript. Our laboratory has significant experience in carrying out this type of experiment and as such we would be very happy to perform them. We will reintroduce siRNA-resistant SUR1 following knockdown of endogenous SUR1 levels and confirm that E6/E7 expression and proliferation are restored.

CROSS-CONSULTATION COMMENTS I note several areas of common feedback among the reviews. Several reviewers commented on the large number of experiments and that the work is of interest to researchers working on HPV and cancer therapeutics. Several reviewers shared concerns about cell viability upon HPV oncoprotein knockdown and about toxicity in various experiments. Several reviewers also raised concerns about the validation of SUR1 protein levels in several experiments. These concerns seem to me to be critical to address to strengthen the manuscript. I note that Reviewer #3's suggestion of making E7 knockout cells (presumably in HPV+ cancer cell lines) is unlikely to be possible because the cells require E7 for survival.

We agree that the two main areas of concern shared among the reviewers (cell viability assays and validation of SUR1 protein levels) are issues that should be addressed in a revised version of this manuscript. We will endeavour to perform the experiments described above, which we hope will significantly enhance the impact of our work.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): Major Comments: Authors did not explain how HPV E7 would upregulate ABCC8 transcription or elevate SUR1 protein (Figure 4). Depletion of E7 is known to produce lethal effect in cervical cancer cell lines. No experiment was done to assess cytotoxicity. Hence it is not clear from the available evidence if the SUR1 is reduced by direct E7 mediated event or indirectly by general cytotoxicity induced by E7 knock down.

We thank the reviewer for their suggestions. We agree that it would be useful to provide some mechanistic insight into how E7 upregulates ABCC8 transcription. We therefore plan to analyse the promoter region of ABCC8 to identify potential transcriptional regulators. ChIP-qPCR and luciferase reporter constructs containing the ABCC8 promoter region will be used to unravel the importance of any candidate TFs identified. An assessment of the impact of E7 on the expression and/or activity of these TFs may also be performed. Finally, we will combine E7 overexpression in a HPV- cell line with knockdown/inhibition of a candidate TF to confirm our findings.

Experiments to assess cell viability/cytotoxicity will be performed as outlined in our response to Reviewer #1.

Authors did not analyze expression level and role of p53, pRB proteins, the direct targets of E6 and E7 proteins, on cell cycle regulation following SUR1 siRNA or Glibenclamide-treatment in cervical cancer cell lines.

We agree that the protein levels of p53 and pRb, the primary targets of E6 and E7 respectively, should be analysed in HeLa and SiHa cells following SUR1 knockdown and glibenclamide treatment and will endeavour to perform this.

Minor Comments:

Additional immunofluorescence or histological analysis is necessary to assess the potential cytotoxic effects of E7 siRNA, SUR1 siRNA or KATP inhibitors (Glibenclamide) in cervical cancer cell lines.

We agree that an assessment of cell viability will strengthen the manuscript and we plan to address this as outlined in our response to Reviewer #1.

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

In addition to the points raised by the reviewers, we identified a minor error that occurred during assembly of the manuscript. Incorrect images of colony formation assays were provided in the original version of Figure 5B. This has now been amended in the transferred manuscript.

__Reviewer #1 (Evidence, reproducibility and clarity (Required)):____ __Overall, the data are of high quality and the individual results are consistent with each other and are convincing. However, the authors have understandably focused on two HPV-positive cancer cell lines (affected by modulating KATP levels) and one HPV-negative cancer cell line (which is not affected in the same way). The ability to extrapolate to conclusions about cervical or HPV-positive cancers in general is therefore limited and many of the authors' statements should be tempered to reflect the experiments they have conducted.

We thank the reviewer for their positive comments regarding our data. We agree that by mainly focussing our studies on cervical cancer cell lines, we limit the potential for extrapolation to other HPV-associated malignancies. We were careful to qualify many of our statements in the original submission to reflect this: e.g. lines 314-315: “Collectively, these data demonstrate that KATP channels are important drivers of proliferation in HPV+ cervical cancer cells.” Post review, we have altered references to HPV+ cancers in general to more accurately reflect the data presented, as outlined below:

• Lines 112-113: We hope that the targeting of KATP channels may prove to be beneficial in the treatment of HPV-associated __cervical __neoplasia.____

• Lines 430-431: As such, we believe that the clinically available inhibitors of KATP channels could constitute a potential novel therapy for HPV-associated malignancies HPV+ cervical cancer.

  Addressing the following major points would help to strengthen the impact of the work:

• The paper would be greatly strengthened by addressing whether knockdown of SUR1 and knockdown of E6/E7 are affecting cell viability. siRNA depletion of E6 and E7 will cause HeLa and SiHa cells to senesce; at what time point post knockdown were the experiments performed? Is it possible to perform CellTiterGlo or other cell viability assays to confirm that the phenotypes observed upon E6/E7 depletion and upon SUR1 depletion or drug treatment are not the result of cell death/senescence/toxicity?

All experiments involving siRNA-mediated knockdown were performed at 72 hours post-transfection. We apologise for omitting this information, and it has now been added to the ‘Materials and Methods’ section.

Minor comments: The text and figures are clear and statistics are appropriate. The authors should include at what time point post siRNA transfection the experiments were conducted.

As above, this information has been added to the ‘Materials and Methods’ section.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)):____ __E6 and E7 protein bands in DMSO treated HeLa and SiHa cells are not consistent between Figures 1 E, H and J, hence confound the interpretation. There is no information on biological replicates. It is not clear why the data from inhibitor treatments were not corroborated by genetic knock down or knock out experiments.

Regarding the number of biological replicates, as described under the ‘Statistical analysis’ subheading of the ‘Materials and Methods’ section, “all experiments were performed a minimum of three times, unless stated otherwise”. Where data is presented as bar graphs, this information is also included in the figure legend and each biological replicate is represented by a single data point where possible. In the case of western blots, a statement of the number of biological repeats has been added under the ‘Western blot analysis’ subheading of the ‘Materials and Methods’ section:

• Lines 614-615: “A minimum of three biological repeats were performed in all cases and representative blot images are displayed.”

  Minor Comments: They did not provide physiological functions of K+ATP channel. I consider this information should be important part of the introduction.

We agree that this would provide important contextual information and apologise for omitting this in the original submission. Details of some well-characterised functions of KATP channels, outside of their potential role in regulating cell proliferation, have been added to the introduction (lines 99-102).

The evidence for elevated expression of SUR1 in raft cultures of uninfected and HPV-18 infected HFK, CINs, and HSIL like cultures of W12E cells (Figure 2) is not of good quality. Moreover, in the absence of histological evidence (hematoxylin and eosin staining) and markers for HPV E6 E7 activity it is difficult to interpret about the location of SUR1 signals in spatial relationship to E7 functions.

In an attempt to resolve the issue highlighted, we have removed a reference in the text to the layers of the epithelium in which SUR1 expression is upregulated, as detailed below:

• Lines 195-197: This demonstrated a marked increase in SUR1 protein expression in __the suprabasal layers of __HPV18+ rafts in comparison to NHK raft cultures, consistent across both donors (Fig 2C).

  There is no physical evidence that HPV-18 transfected HFK indeed harbored HPV-18 plasmid in this experiment. What is the effect of glibenclamide on HPV-18 episome maintenance or replication?

The HPV18-containing keratinocytes used in this study are the same model system we have used in previous investigations (Wasson et al. (2017) Oncotarget 8(61): 103581–103600; Morgan et al (2018) PLoS Pathog 14(4): e1006975). In these studies, which focus on the HPV life cycle rather than HPV+ cancer, Southern blot analysis of HPV episomes and western blots for E6/E7 protein levels were performed, providing validation of the presence of HPV in these cells. We have added a reference to our previous work in the text (line 191).

As this manuscript primarily focusses on HPV+ cancer rather than HR-HPV infection, we believe an assessment of the role of KATP channels on HPV episome maintenance and/or genome replication to be beyond the scope of this study.

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

__Reviewer #1 (Evidence, reproducibility and clarity (Required)):____ __Addressing the following major points would help to strengthen the impact of the work:

The authors should address the idea of off-target effects, either experimentally or, more feasibly, by discussing the possibility of non-specific effects of SUR1 knockdown. They use a pool of four siRNAs to SUR1 and the risk of off-target effects would be greatly reduced if individual siRNAs were tested and shown to have the same effect as one another. Similarly, several experiments use just one shRNA, limiting the ability to draw conclusions.

Our plan to address potential off-target effects of the siRNAs used is outlined above. Regarding the shRNA data, we use two different shRNAs in the majority of experiments presented. These were found to have highly similar impacts on E6/E7 expression (Figure 3E & 3G) and proliferation (Supp Figure 4). We therefore do not believe that further experiments to eliminate off-target effects of the shRNA are necessary.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)):____ __Major Comments: Overall, the authors performed many experiments to reveal an interesting and novel mechanism. (1) SUR1 expression and activity is necessary for HPV16 and-18 E6 and E7 expression. (2) HPV-16/18 E7 upregulates expression of ABCC8/SUR1 transcription. (3) SUR1 containing K+ATP channel then phosphorylates ERK. (4) Activated ERK then phosphorylates JUN/AP1. (5) Next, activated JUN/AP1 promotes E7 or E6E7 expression from HPV URR. However, in this cyclic feedforward regulation of these genes there is no control mechanism. Then how is homeostasis maintained in HPV infected lesions?

We thank the reviewer for praising the “interesting and novel mechanism” we have uncovered. The primary focus of our study is HPV+ cervical cancers, rather than HPV-infected lesions. The data we present in Figure 2 indicates that upregulation of KATP channel expression and/or activity is likely also occurring during HR-HPV infection, given we see e.g. increased SUR1 staining in HPV18-containing organotypic rafts. However, given our primary focus, we believe a more thorough assessment of KATP channels in HR-HPV infection, including any potential homeostatic regulation mechanisms, is outside the scope of our current study and inclusion of additional life cycle data would dilute the main conclusions of this manuscript. It is nonetheless a potentially exciting area for future work, and could form part of a separate, focussed manuscript.

E6 and E7 protein bands in DMSO treated HeLa and SiHa cells are not consistent between Figures 1 E, H and J, hence confound the interpretation. There is no information on biological replicates. It is not clear why the data from inhibitor treatments were not corroborated by genetic knock down or knock out experiments.

We believe that bands for E6 and E7 protein in DMSO-treated samples in Figure 1E and 1J are broadly consistent. However, we appreciate that E6 and E7 protein expression appears to be lower in DMSO samples in Figure 1H. All experiments involving diazoxide stimulation were performed under conditions of serum starvation, as indicated in the legends for Figures 1 and 8. Oncoprotein expression is known to be regulated by a series of host transcription factors, many of which become active in response to growth factor stimulation, such as AP-1 and SP1 (see: Tan et al. (1992) Nucleic Acids Res. 20(2):251-6; Hoppe-Seyler et al. (1992) Nucleic Acids Res. 20(24):6701-6; Butz K et al. (1993) J Virol. 67(11):6476-86). Serum starvation was therefore used to disentangle the upregulation of HPV gene expression by KATP channels from the myriad of other host signalling pathways demonstrated to drive E6/E7 expression. A side effect of this was a reduction in basal E6 and E7 protein levels in DMSO-treated cells. In addition, shorter exposure times were deliberately selected to prevent overexposure of protein bands corresponding to 50uM diazoxide treated cells. We apologise for any confusion caused.

Data from inhibitor treatments has been corroborated by knockdown experiments throughout the manuscript. The loss of E6/E7 expression with glibenclamide treatment was confirmed by SUR1 siRNA and shRNA knockdowns (Figure 3D-G) and Kir6.2 knockdown (Supp Figure 3C-D). The glibenclamide-induced loss of proliferation observed in HeLa and SiHa cells was also validated using the same approaches (Figure 5D-F, Supp Figure 3E-G, Supp Figure 4). Indeed, the cell cycle dysregulation experiments in Figure 7 were all performed with both inhibitor treatments and SUR1 siRNA knockdown.

The increase of G1 population, determined by flow cytometry, of HeLa cells treated with Glib or SUR1 siRNA is relative to controls appears to be small and not supported by similar study on other HPV+ or HPV_ vervical cancer cell lines. Importantly the mechanism of this increased G1 in HeLa cell line is not clear. The immunoblot data about the role of cyclins are not sufficient.

The flow cytometry experiments with glibenclamide treatment and SUR1 knockdown in HeLa cells were also performed with HPV16+ SiHa cells (Figure 7A-B) and the effects are highly consistent between the two cell lines. We believe that elucidating a more detailed mechanism of the observed G1 arrest is beyond the scope of this manuscript. Analysis of the mRNA and protein expression of cyclins was intended to provide corroboration of our findings via flow cytometry (i.e. a specific reduction in G1-phase cyclins corresponds to an accumulation of cells in G1 phase), rather than provide mechanistic insight.

What is the physiological effect of cyclin D1 in the context of HR-HPV infection (Figure 7)? In the event of HPV E7 mediated pRB degradation in cervical cancer cell lines, the inactivation of pRB by cyclin D1 does not appear to be physiologically relevant, may not account for difference in growth. It is known in literature that Cyclins A2 and B1 are often elevated by E7 activity. If SUR1 siRNA reduces E7-transcription and protein levels as shown in earlier results, why cyclinB1 and A2 protein level did not change?

As discussed, this manuscript primarily focusses on the role of KATP channels in HPV+ cervical cancer cells. An investigation into the effects on cyclin D1 expression in the context of HR-HPV infection, whilst an important question, is beyond the scope of this study and should form part of a standalone manuscript.

Regarding the expression of cyclins A2 and B1, we repeatedly observed very little impact following glibenclamide treatment and SUR1 knockdown in both cell lines examined. As highlighted above, given we observe a G1 arrest after KATP channel knockdown/inhibition, it would perhaps be unusual to observe changes in the expression of cyclins which drive G2 and M phase progression, respectively.

If activated ERK1/2 and c-Jun is required for URR activity, why are not they detectable in DSO or scrRNA treated HeLa cells (Fig 8A, B)? Why there is no 18 E7 in DMSO treated HeLa cells (Fig. 8A)? Authors also did not explain how inhibition of KATP channel regulates ERK phosphorylation in cervical cancer cell lines. There is no data from additional cervical cancer cell lines or HSIL mimicking W12E.

As mentioned above and as referred to in the figure legend, the experiment presented in Figure 8A was performed under serum starved conditions. Thus, the levels of phosphorylated ERK1/2 and cJun are much reduced in the unstimulated, DMSO-treated cells. Importantly, cJun/AP-1 is capable of activating its own expression, explaining the low total protein level of cJun in this sample. Further, as has widely been reported, MAPK signalling and AP-1 activity are critical drivers of HPV URR-driven transcription (e.g., see: Morgan et al. (2021) Cell Death Differ. 28(5):1669-87), so the reduced signalling activity resulting from serum starvation will consequently lower 18E7 expression. Shorter exposure times were selected for the pERK1/2, p-cJun and cJun western blots in Figure 8B to highlight the dramatic increase in pathway activation following KATP channel overexpression and for consistency with Figure 8A. We apologise for any confusion caused but do not believe that the potential issue raised here significantly alters any of the conclusions drawn.

We believe that an explanation of the mechanism by which KATP channel activity contributes to the activation of ERK1/2 signalling in HPV+ cervical cancer cells is beyond the scope of this initial publication. In the course of acquiring the data presented here, we aimed to provide some evidence of how KATP channels regulate proliferation in these cells, and therefore decided to investigate what impact they had on host cell signalling pathways known to be critical for proliferation. This led to us identifying enhanced ERK1/2 activity in response to KATP channel stimulation/overexpression. We agree that the critical next step will be to elucidate how channels promote ERK1/2 signalling, but this would require a significant body of work and as such would warrant being in a standalone or follow-up publication.

Throughout the manuscript, we endeavoured to validate our discoveries in the HPV18+ HeLa cell line in an additional cervical cancer cell line (HPV16+ SiHa cells). We provide evidence that the requirement for KATP channel activity is shared by both cell lines, and the impacts on oncoprotein expression, proliferation and cell cycle progression are highly concordant between the two cell lines. Thus, it is reasonable to assume that the mechanism by which KATP channels drive proliferation and HPV URR activity, elucidated in Figure 8 using HeLa cells, will be common to other HPV+ cervical cancer cell lines. Given the wealth of evidence supporting our proposal in Figure 8, and the highly concordant data presented earlier in the manuscript, we do not believe repeating all of the experiments in Figure 8 in a HPV16+ cell line is warranted. Similarly, as this manuscript focusses on HPV+ cancer, we believe that a study of the activation of MAPK/AP-1 signalling by KATP channels in HSIL mimicking W12E cells is beyond the scope of this paper and should constitute part of a standalone manuscript.

Minor Comments: In introduction, the authors mentioned that high risk HPV E6 and E7 deregulate cell cycle in host cells, and current limitations in cervical cancer treatments. Then they introduced importance of K+ ion channels in cell cycle regulation by sighting published literature not related to HPV, immediately followed by their proposed study on role of K+ATP channels in HPV infection. However, authors did not sufficiently clarify the rational of taking up a study on K+ channels in the context of HPV infection or E6 and E7 expression. If K+ATP channel proteins are elevated by E7, it is highly likely that there are some prior information on status of these transporters in the published literature or data from RNAseq analyses.

As the reviewer acknowledges, we described in the introduction the importance of K+ channels in regulating cell proliferation and the absence of effective HPV-specific therapies. We also stated that “ion channels may represent ideal candidates for … novel therapies given the abundance of licensed and clinically available drugs targeting the complexes which could be repurposed…”. Thus, the rationale for studying K+ channels in HPV+ cancers was to see if any of the available inhibitors of K+ channels could potentially be repurposed to be used in treating HPV-driven cervical cancer. We believe this logic is explained with sufficient clarity in the original draft.

Regarding prior analysis of KATP channel expression, in Figure 2H of the manuscript we analyse a publically available microarray dataset, which provides mRNA expression data for 128 cervical tissue specimens (24 normal, 14 CIN1 lesions, 22 CIN2 lesions, 40 CIN3 lesions, and 28 cancers specimens). ABCC8 expression was found to be significantly higher in the CIN3 and cervical cancer specimens, compared to normal samples. Details of the dataset used are provided in the ‘Materials and Methods’ section.

The evidence for elevated expression of SUR1 in raft cultures of uninfected and HPV-18 infected HFK, CINs, and HSIL like cultures of W12E cells (Figure 2) is not of good quality. Moreover, in the absence of histological evidence (hematoxylin and eosin staining) and markers for HPV E6 E7 activity it is difficult to interpret about the location of SUR1 signals in spatial relationship to E7 functions.

Organotypic raft culture data was included to demonstrate increased SUR1 expression in primary keratinocytes containing HR-HPV to show broader upregulation of the host factor and strengthen data from cell lines and clinical samples. Our data shows an upregulation of SUR1 in the HPV-containing rafts compared to controls. However, raft culture is a highly complex, time-consuming and expensive technique to perform. Therefore, whilst we agree, in principal, that being able to more closely correlate the increase in SUR1 protein levels to specific layers of the epithelium (e.g. via H&E staining and for markers of E6/E7 activity) would be of value, we would not be able to perform these assays within a reasonable time frame. Moreover, we feel that it would not add significant new knowledge to the study of SUR1 in the context of HPV-driven cancers.

There is no physical evidence that HPV-18 transfected HFK indeed harbored HPV-18 plasmid in this experiment. What is the effect of glibenclamide on HPV-18 episome maintenance or replication?

As this manuscript primarily focusses on HPV+ cancer rather than HR-HPV infection, we believe an assessment of the role of KATP channels on HPV episome maintenance and/or genome replication to be beyond the scope of this study.

Reviewer #2 (Significance (Required)):____ (1) General Assessment: Strengths and limitations This study identified KATP channel components as novel regulators of transcriptional activity of high-risk HPV-18 URR through ERK1/2-c-Jun/AP1 pathway. Authors revealed that HPV E7 regulates expression of ABCC8, the gene for channel component SUR1 protein.

There are important limitations. (1) Lack of any information about homeostatic regulation of SUR1 in HPV infection, (2) Lack of sufficient evidence about potential confounding cytotoxic effects of SUR1 inhibition or E7 down regulation on cervical cancer cells. (3) Immunoblot experiments are not consistent. (4) There is no mechanism of how E7 regulates ABCC8 transcription. (5) What is the mechanism for SUR1 regulate cell cycle in HPV+ cells? (6) There is no mention of effect of SUR1 on cell cycle regulators p53 and pRB, which are direct targets of HPV E6 and E7 proteins. (7) There is no evidence for the role of Kir6.2 /SUR1 in the regulation of HPV-16 URR, which causes most of HPV-attributed cancers. (8) Authors did not analyze spatial relationship between HPV E6 and E7 activity and expression of SUR1 protein in raft cultures of human foreskin keratinocytes with or without E6E7 expression and in cervical cancer tissue.

We thank the reviewer for summarising in a concise manner the areas of this manuscript they believe could be improved. Our responses to points 1-6 and point 8 have been detailed above. Regarding (7), we present data showing that KATP channel inhibition/knockdown negatively affects E6 and E7 expression in HPV16+ SiHa cells (Figure 1D-E, Figure 3D and F, Supp Figure 3C-D). Furthermore, we present evidence that SUR1 knockdown in SiHa cells correlates with a reduction in HPV16 URR-driven luciferase activity (Figure 3H). We therefore believe that this issue was adequately addressed in the original manuscript.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)):____ __Minor comments:

Knockout SUR1 stable cell lines and knockout HPV E7 stable cell lines should be established to test all the related data.

We have performed experiments using two well characterised inhibitors of KATP channels (glibenclamide and tolbutamide) and both siRNA- and shRNA-mediated knockdown of SUR1, all of which result in similar reductions in HPV E6/E7 expression. Further, the reductions in proliferation observed in HPV+ cell lines following glibenclamide treatment or siRNA/shRNA knockdown of SUR1 are also highly concordant. Thus, we do not believe the establishment of knock__out__ cell lines, using e.g. CRISPR/Cas9 technology, would significantly enhance the manuscript, particularly given the time and expense involved in this.

As noted by Reviewer #1 following cross-consultation, the establishment of E7 knockout cells lines is “unlikely to be possible because the cells require E7 for survival”. It has been previously demonstrated that in the absence of E7 expression, HeLa cells cease to proliferate and undergo senescence within 10 days (see: DeFelippis et al. (2003) J.Virol 77(2): 1551–1563). We therefore agree with Reviewer #1 and believe that, unfortunately, we would be unable to carry out the suggested experiment.

Tumor weights of the in vivo experiment should be indicated.

Tumour weights were not collected following the conclusion of the in vivo experiment, so we are unable to provide this information. The experiment was designed such that animals would be sacrificed upon the tumours reaching a set measurement (15 mm in either direction), rather than concluding the experiment at a set end point. Therefore, many of the tumours would have been of similar weight upon sacrifice, but critically the SUR1-depleted tumours took significantly longer to reach that size. We therefore believe that, given the experimental set-up, adding the tumour weights would not add significant value, even if we were able to provide this information.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

Authors present the evidence that HPV can target ATP-sensitive potassium ion (KATP) channels of a host to promote cervical carcinogenesis. They indicate that these channels are active in HPV-positive cells and that this activity is required for HPV oncoprotein expression by using activators and inhibitors of KATP channels. Furthermore, they verified SUR1 was upregulated in both HPV+ cervical cancer cells and in clinical samples in a manner dependent on the E7 oncoprotein. Knockdown of SUR1 or KATP channel inhibition significantly impeded cell proliferation via induction of a G1 cell cycle phase arrest. They propose that tumorgenesis effect of KATP channels is mediated via the activation of a MAPK/AP-1 signalling axis. Overall, It is an interesting research to unveil the mechanism how HPV promote cervical carcinogenesis through ATP-sensitive potassium ion channels. However，some major concerns should be addressed.

Major comments:

• Are the key conclusions convincing?

I think the key conclusions are convincing. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

NO - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

NO - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. - Are the data and the methods presented in such a way that they can be reproduced?

Yes - Are the experiments adequately replicated and statistical analysis adequate?

The experiments are adequately replicated and statistical analysis

Minor comments:

• Specific experimental issues that are easily addressable.

Yes - Are prior studies referenced appropriately?

Yes - Are the text and figures clear and accurate?

yes - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Knockout SUR1 stable cell lines and knockout HPV E7 stable cell lines should be established to test all the related data.

Tumor weights of the in vivo experiment should be indicated.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The author explain for the first time that HPV can upregulate host ATP-sensitive potassium ion channels, consequently activate MAPK/AP-1 signalling contribute to cervical carcinogenesis. This is a new mechanism how HPV cause cervical carcinogenesis. However, the MAPK/AP-1 signalling contributes to carcinogenesis is well known. The technical in the experiment is commonly used. - Place the work in the context of the existing literature (provide references, where appropriate).

HPV can promote cervical carcinogenesis through different pathway including MAPK/AP-1(1: Wang M, Qiao X, Cooper T, Pan W, Liu L, Hayball J, Lin J, Cui X, Zhou Y,Zhang S, Zou Y, Zhang R, Wang X. HPV E7-mediated NCAPH ectopic expression regulates the carcinogenesis of cervical carcinoma via PI3K/AKT/SGK pathway. Cell Death Dis. 2020 Dec 11;11(12):1049. doi: 10.1038/s41419-020-03244-9. PMID:33311486; PMCID: PMC7732835. 2. Singh T, Chhokar A, Thakur K, Aggarwal N, Pragya P, Yadav J, Tripathi T, Jadli M, Bhat A, Gupta P, Khurana A, Chandra Bharti A. Targeting Aberrant Expression of STAT3 and AP-1 Oncogenic Transcription Factors and HPV Oncoproteins in Cervical Cancer by Berberis aquifolium. Front Pharmacol.2021 Oct 28;12:757414. doi: 10.3389/fphar.2021.757414. PMID: 34776976; PMCID: PMC8580881.). However, the detail mechanism is still elusive. Here, authors indicated E7 can upregulate SUR1, one component of ATP-sensitive potassium ion channels and activate MAPK/AP-1. SUR1 can also upregulat E7 levels. They set up a positive feedback loop to contribute cervical cancer. - State what audience might be interested in and influenced by the reported findings.

cervical carcinogenesis researchers and cancer drug researches. - 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 familiar with cancer related signaling pathway and cancer chemoprevention research. Especially MAPK signaling pathway and related drugs.

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Referee #2

Evidence, reproducibility and clarity

Summary: Authors explored the role of k+ channel transporters in HPV induced cervical cancers. They used several inhibitors and gene knockdowns in biochemical and cell biology experiments to show that SUR1 and Kir6.2 components of K+ ATP channel, via activating pERK1/2 and c-Jun/AP1, up-regulate HPV URR promoter mediated expression of E6 and E7 proteins. They showed that SUR1 knockdown inhibited growth of HeLa cells in vivo.

Major Comments:

Overall, the authors performed many experiments to reveal an interesting and novel mechanism. (1) SUR1 expression and activity is necessary for HPV16 and-18 E6 and E7 expression. (2) HPV-16/18 E7 upregulates expression of ABCC8/SUR1 transcription. (3) SUR1 containing K+ATP channel then phosphorylates ERK. (4) Activated ERK then phosphorylates JUN/AP1. (5) Next, activated JUN/AP1 promotes E7 or E6E7 expression from HPV URR. However, in this cyclic feedforward regulation of these genes there is no control mechanism. Then how is homeostasis maintained in HPV infected lesions?

E6 and E7 protein bands in DMSO treated HeLa and SiHa cells are not consistent between Figures 1 E, H and J, hence confound the interpretation. There is no information on biological replicates. It is not clear why the data from inhibitor treatments were not corroborated by genetic knock down or knock out experiments.

Authors did not explain how HPV E7 would upregulate ABCC8 transcription or elevate SUR1 protein (Figure 4). Depletion of E7 is known to produce lethal effect in cervical cancer cell lines. No experiment was done to assess cytotoxicity. Hence it is not clear from the available evidence if the SUR1 is reduced by direct E7 mediated event or indirectly by general cytotoxicity induced by E7 knock down.

The increase of G1 population, determined by flow cytometry, of HeLa cells treated with Glib or SUR1 siRNA is relative to controls appears to be small and not supported by similar study on other HPV+ or HPV_ vervical cancer cell lines. Importantly the mechanism of this increased G1 in HeLa cell line is not clear. The immunoblot data about the role of cyclins are not sufficient.

What is the physiological effect of cyclin D1 in the context of HR-HPV infection (Figure 7)? In the event of HPV E7 mediated pRB degradation in cervical cancer cell lines, the inactivation of pRB by cyclin D1 does not appear to be physiologically relevant, may not account for difference in growth. It is known in literature that Cyclins A2 and B1 are often elevated by E7 activity. If SUR1 siRNA reduces E7-transcription and protein levels as shown in earlier results, why cyclinB1 and A2 protein level did not change?

Authors did not analyze expression level and role of p53, pRB proteins, the direct targets of E6 and E7 proteins, on cell cycle regulation following SUR1 siRNA or Glibenclamide-treatment in cervical cancer cell lines.

If activated ERK1/2 and c-Jun is required for URR activity, why are not they detectable in DSO or scrRNA treated HeLa cells (Fig 8A, B)? Why there is no 18 E7 in DMSO treated HeLa cells (Fig. 8A)? Authors also did not explain how inhibition of KATP channel regulates ERK phosphorylation in cervical cancer cell lines. There is no data from additional cervical cancer cell lines or HSIL mimicking W12E.

Minor Comments:

In introduction, the authors mentioned that high risk HPV E6 and E7 deregulate cell cycle in host cells, and current limitations in cervical cancer treatments. Then they introduced importance of K+ ion channels in cell cycle regulation by sighting published literature not related to HPV, immediately followed by their proposed study on role of K+ATP channels in HPV infection. However, authors did not sufficiently clarify the rational of taking up a study on K+ channels in the context of HPV infection or E6 and E7 expression. If K+ATP channel proteins are elevated by E7, it is highly likely that there are some prior information on status of these transporters in the published literature or data from RNAseq analyses. They did not provide physiological functions of K+ATP channel. I consider this information should be important part of the introduction.

The evidence for elevated expression of SUR1 in raft cultures of uninfected and HPV-18 infected HFK, CINs, and HSIL like cultures of W12E cells (Figure 2) is not of good quality. Moreover, in the absence of histological evidence (hematoxylin and eosin staining) and markers for HPV E6 E7 activity it is difficult to interpret about the location of SUR1 signals in spatial relationship to E7 functions.

Additional immunofluorescence or histological analysis is necessary to assess the potential cytotoxic effects of E7 siRNA, SUR1 siRNA or KATP inhibitors (Glibenclamide) in cervical cancer cell lines

There is no physical evidence that HPV-18 transfected HFK indeed harbored HPV-18 plasmid in this experiment. What is the effect of glibenclamide on HPV-18 episome maintenance or replication?

Significance

(1) General Assessment: Strengths and limitations

This study identified KATP channel components as novel regulators of transcriptional activity of high-risk HPV-18 URR through ERK1/2-c-Jun/AP1 pathway. Authors revealed that HPV E7 regulates expression of ABCC8, the gene for channel component SUR1 protein.

There are important limitations. (1) Lack of any information about homeostatic regulation of SUR1 in HPV infection, (2) Lack of sufficient evidence about potential confounding cytotoxic effects of SUR1 inhibition or E7 down regulation on cervical cancer cells. (3) Immunoblot experiments are not consistent. (4) There is no mechanism of how E7 regulates ABCC8 transcription. (5) What is the mechanism for SUR1 regulate cell cycle in HPV+ cells? (6) There is no mention of effect of SUR1 on cell cycle regulators p53 and pRB, which are direct targets of HPV E6 and E7 proteins. (7) There is no evidence for the role of Kir6.2 /SUR1 in the regulation of HPV-16 URR, which causes most of HPV-attributed cancers. (8) Authors did not analyze spatial relationship between HPV E6 and E7 activity and expression of SUR1 protein in raft cultures of human foreskin keratinocytes with or without E6E7 expression and in cervical cancer tissue.

(2) Advance: This study identifies SUR1/Kir6.2 as new targets to intervene HPV-18 URR activity and demonstrates potential to inhibit growth of cervical cancer tumors using HeLa xenograft model. This study did not develop any new methodology, novel mutation or model system.

(3) Audience: This study is aimed at basic scientists involved in the field of HPV research.

(4) Describe your expertise. I have long experience in HPV research. I study regulation of HR-HPV18 life cycle in 3D organotypic raft cultures of HPV-18 infected neonatal foreskin keratinocytes. A major part of my research is focused on identification of novel therapeutics against cervical cancers using in vitro 3D organoids and in vivo PDX models.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript by Scarth and colleagues, the authors investigate the relationship between ATP-sensitive potassium ion channels (KATP) and the viability and growth of certain HPV-positive cancer cell lines. In a series of detailed and carefully conducted experiments, they determine that there is a correlation between KATP channel activity and levels of certain HPV E6 and E7 RNA and protein. KATP channels are active in HeLa cells. In HeLa and SiHa cells, inhibiting KATP activity decreases HPV oncoprotein levels. HPV-positive status in the cell lines examined is found to be associated with an upregulation of the ABCC8 gene, which encodes the SUR1 KATP subunit, and some of the data supports that SUR1 protein levels increase with cervical cancer CIN grade. Depleting SUR1 with shRNA or siRNA reduces KATP activity and decreases HPV E6 and E7 levels in HeLa and SiHa cells. The opposite is also true; depleting ABCC8 reduces the levels of HPV E6 and E7 transcripts. The effect on ABCC8 appears to be due mainly to the effects of HPV E7. Decreased KATP activity is associated with decreased growth of HeLa and SiHa cells in monolayer and in anchorage independent growth assays, perhaps not surprising given that E6/E7 levels are reduced in the cells under the treatment conditions. SUR1 overexpression itself promotes cell growth even in the absence of HPV oncoproteins. The growth defect upon KATP inhibition or siSUR1 is associated with some modest cell cycle dysregulation and, impressively, with reduced tumor growth in a mouse model. Finally, the authors present evidence that increased KATP activity is associated with increased recruitment of the transcription factor AP-1 to the HPV18 promoter and enhancer.

Overall, the data are of high quality and the individual results are consistent with each other and are convincing. However, the authors have understandably focused on two HPV-positive cancer cell lines (affected by modulating KATP levels) and one HPV-negative cancer cell line (which is not affected in the same way). The ability to extrapolate to conclusions about cervical or HPV-positive cancers in general is therefore limited and many of the authors' statements should be tempered to reflect the experiments they have conducted.

Addressing the following major points would help to strengthen the impact of the work:

1. The paper would be greatly strengthened by addressing whether knockdown of SUR1 and knockdown of E6/E7 are affecting cell viability. siRNA depletion of E6 and E7 will cause HeLa and SiHa cells to senesce; at what time point post knockdown were the experiments performed? Is it possible to perform CellTiterGlo or other cell viability assays to confirm that the phenotypes observed upon E6/E7 depletion and upon SUR1 depletion or drug treatment are not the result of cell death/senescence/toxicity?
2. There is a major concern regarding whether SUR1 protein is produced at a biologically relevant level in SiHa and HeLa cells, in which most of the experiments in the paper were conducted. Protein levels are assessed in Fig 2 by immunostaining in raft cultures and in a cervical cancer tissue microarray. However, protein levels are otherwise not examined, especially in SiHa and HeLa cells. Is SUR1 protein produced in these cells? Are its levels reduced by the knockdown approaches? The fold change RNA data presented in figure 2A does not convincingly address this question, since even an 8-fold increase of ABCC8 mRNA over a low background level might not have biological significance. It would be very helpful to measure SUR1 protein in several of the experiments in HeLa and SiHa cells.
3. The authors should address the idea of off-target effects, either experimentally or, more feasibly, by discussing the possibility of non-specific effects of SUR1 knockdown. They use a pool of four siRNAs to SUR1 and the risk of off-target effects would be greatly reduced if individual siRNAs were tested and shown to have the same effect as one another. Similarly, several experiments use just one shRNA, limiting the ability to draw conclusions.
4. Finally, since many of the experiments rely on knockdown approaches that show similar readouts, a rescue experiment (restore sh or si-resistant SUR1 and assess the impact on the phenotype) would confirm that the effects being observed are due to changes in SUR1 levels and not to off-target effects.

It is recognized that some of these experiments would be lengthy and technically challenging to perform. Measuring cell viability and SUR1 protein levels in SiHa and HeLa cells should be relatively straightforward. The experiments to address off-target effects (rescue experiment, deconvolving siRNA pool) are more involved. If it is not possible to complete such experiments, the possibility of off-target effects should be discussed in the text.

Minor comments:

The text and figures are clear and statistics are appropriate. The authors should include at what time point post siRNA transfection the experiments were conducted.

Referees cross-commenting

I note several areas of common feedback among the reviews. Several reviewers commented on the large number of experiments and that the work is of interest to researchers working on HPV and cancer therapeutics. Several reviewers shared concerns about cell viability upon HPV oncoprotein knockdown and about toxicity in various experiments. Several reviewers also raised concerns about the validation of SUR1 protein levels in several experiments. These concerns seem to me to be critical to address to strengthen the manuscript. I note that Reviewer #3's suggestion of making E7 knockout cells (presumably in HPV+ cancer cell lines) is unlikely to be possible because the cells require E7 for survival.

Significance

The work connects the biology of certain cervical cancer cell lines to KATP channels. It will be of interest to HPV researchers and to cancer researchers whose interests involve KATP signaling. As a reviewer, I have expertise in HPV biology but not in KATP signaling.

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Reply to the reviewers

Manuscript number: RC-2022-01673

Corresponding author(s): Eric Shoubridge

[Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

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1. General Statements [optional]

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2. Point-by-point description of the revisions

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

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

*In this MS, Scheuttpelz et al demonstrate that SLC25A46, a novel member of the mitochondrial carrier protein family localized to the outer-mitochondrial membrane, is an important regulator of mitochondrial dynamics. They show that knockout of SLC25A46 results in mitochondrial fragmentation, whereas over-expression of WT SLC25A46 or pathogenic variants/mutants of SLC25A46 results in mitochondria hyperfusion. SLC25A46 might affect fusion/fission directly since it is localized to both mitochondrial fusion and fission sites. Moreover, its loss/expression of variants alters the levels of the high molecular weight complexes of MFN2 and alters the levels of the long/short forms of OPA1. In addition, Scheuttpelz et al show that loss of SLC25A46 results in changes in the mitochondrial lipid profile, suggesting that SLC25A46 might regulate mitochondrial dynamics via regulation of mitochondrial lipid metabolism. Thus, the findings described are novel and exciting, however it remains poorly understood how SLC25A46 localization to fusion/fission sites is related to mitochondrial fusion/fission, and how are these results related to its effect on the MFN2/OPA1 complexes/forms, and to its possible role in regulating lipid metabolism. *

*Specific comments: *

1. *Are the DRP1 and the DRP1-receptor native complexes (appearing in BN-PAGE) altered in the SLC25A46 KO/+pathogenic variants cells? * We have tried to visualize the DRP-1 receptor complexes (MID49, MID51, MFF) on BN-PAGE gels without success. The Western blot in (a) below shows that the steady-state levels of all three receptors are similar under all conditions we tested, but the same antibodies used in this blot did not detect the native complexes on BN-PAGE gels. To our knowledge this has not been done in the literature. We previously reported (Janer et al, 2016) that DRP1 recruitment in patient fibroblasts (T142I) was only slightly reduced and that its oligomerization state (after crosslinking analysis) was slightly increased in the patient cells, which would not explain the mitochondrial hyperfusion.

*Do the pathogenic variants of SLC25A46 localize only to mitochondria? Do they fold similar to the WT protein (i.e., similar prot K cleavage products)? Are they loss- or gain-of-function variants/mutants? *

We previously provided images of all pathogenic variants in Supplementary Figure 1 by decorating with an SLC25A46 antibody; however the low steady-state levels of all but the R257Q variant make visualization difficult. Supplementary Figure 3d shows the R257Q variant with an analysis of its suborganellar localization. We performed a PK assay of R257Q (the most abundant pathogenic variant) and it behaves as the wild-type protein (rescued in knock-out background and in the control cell line) and as the outer membrane protein MFN2. We have now performed an alkaline carbonate extraction assays showing that all pathogenic variants (T142I, R257Q and E335D) are integral membrane proteins. (results shown below)

All described SLC25A46 mutations are loss-of-function biallelic missense, STOP or frameshift mutations, and where it has been investigated, all are associated with reduced steady-state levels of SLC25A46 protein compared to controls. The level of residual SLC25A46 protein correlates with disease severity Abrams et al. (2018).

Proteinase K Assay and Alkaline Carbonate Extraction show an integral insertion of SLC25A46 and its pathogenic variants into the outer membrane.

a) Proteinase K digestion assay of mitochondria from control fibroblasts or SLC25A46 knock-out fibroblasts with reintroduced wild-type protein (+wt) of SLC25A46 or the pathogenic variant R257Q. Mitochondria were exposed to an increasing concentration of proteinase K to determine the submitochondrial localization of SLC25A46. SLC25A46 and its pathogenic variants behave as outer membrane proteins. MFN2 was used as a control for an outer membrane protein, AIF for protein present in the inter‐membrane space, and SCO1 for an inner membrane protein. b) Alkaline carbonate extraction of mitochondria from control fibroblasts or SLC25A46 knock-out fibroblasts with reintroduced wild-type protein (+wt) of SLC25A46 or the pathogenic variants (+T142I, +R257Q, +E335D) . Immunoblot analysis shows that all SLC25A46 variants behave as integral membrane proteins. PRDX3 (soluble mitochondrial matrix protein) and MFN2 (integral outer membrane protein) were used as controls.

*The BN-PAGE results presented in Fig 5 appear without molecular weight markers, and thus the sizes of the complexes are not known. Why did the authors conclude that the bands that appear in the MFN1, MFN2, and OPA1 blots represent monomers and oligomers of these proteins (Fig 5b)? Is it possible that all/part of these immune-reactive bands represent complexes with other proteins and not monomers and/or homo-oligomers? How does SLC25A46 affect the complex state of these proteins if it does not associate with them in the native state, as seen in Fig 5d? *

We added a molecular weight ladder in Figure 5b which was confirmed using the known molecular weights the complexes of the oxidative phosphorylation complexes.

*Fig 5b (MFN2 blot): SLC25A46 KO cells expressing each of the pathogenic variants/mutants of SLC25A46 show different levels of the MFN2-immuoreactive higher molecular weight band (MFN2-HMWB; last three lanes), however all three cell lines show mitochondria hyperfusion. Moreover, the intensity of the MFN2-HMWB in two of these mutant lines (+T142I and +E335D) is similar to the intensity of the band that appears in the SLC25A46 KO cells, cells which show fragmented mitochondria. Thus, there is not a clear correlation between the state of SLC25A46, the levels of the MFN2-HMWB, and the mitochondrial morphology. *

The reviewer is correct and in fact we discusssed this point in the fourth paragraph of the discussion part in our paper: “The oligomerization of both MFN2 and OPA1 was altered by the loss of SLC25A46 function. High molecular weight oligomers of MFN2 were reduced in the null cell line and in the presence of all three pathogenic variants, a reduction that correlated with the steady-state level of residual SLC25A46 protein. Thus, rather unexpectedly MFN2 oligomerization did not correlate with mitochondrial morphology in our model.” It thus appears that the oligermerization state of MFN2 is not the determining factor for the observed changes in mitochondrial morphology.

*The authors' interpretations of the results presented in Fig 5d, arguing that there is a correlation between the appearances of the short/long forms of OPA1 and the fusion/fission state of the different cells, are not convincing. BN-PAGE results can vary between experiments, and thus need to be repeated and accompanied by densitometry analyses, especially in cases where the intensity of the bands (short and long forms of OPA1) seem largely similar in the single experiment presented. *

We have now performed additional two-dimensional electrophoresis (BN-PAGE/SDS-PAGE) analyses and have quantified the results. (a) Mitochondria from control, knock-out, re-expression of wt-SLC25A46 and the pathogenic variant p.T142I were run on a BN-PAGE with additional SDS gel-electrophoreses and immunoblotted against OPA1. (b) Quantification of the high molecular weight complexes (>600 kDa) of OPA1 (indicated in the green boxes in (a) relative to the total signal. (c) Quantification of the relative proportions of the long vs short forms of OPA1 forms in the high molecular weight complexes (>200 kDa) as indicated in the example (d) showing the longer forms of the higher complexes in the yellow box and the shorter forms in the purple box.

OPA1 forms high molecular oligomeric complexes that are altered in SLC25A46 loss of function cells

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

*The manuscript "SLC25A46 localizes to sites of mitochondrial fission and fusion and loss of function variants alter the oligomerization states of MFN2 and OPA1" partially characterizes the outer mitochondrial membrane protein SLC25A46, finding a localization to the tips and branching points of mitochondria and an effect on both mitochondrial internal structure and mitochondrial network dynamics in deletions and expression of specific mutants. The localization was conducted both with tagged protein and antibodies, which is appreciated, as tagging and overexpression can often alter localization of mitochondrial proteins. Interestingly, disease variants have an opposite effect as the deletion in mitochondria network behavior, with fragmented mitochondria in deletion strains and elongated or fused mitochondria in the mutant strains. The paper also finds alteration on membrane composition, and postulates a function in lipid exchange. While the paper falls short of a full functional characterization, the results are reasonable, internally consistent, and promising for future follow-ups. *

*Altered protein expression levels for the disease variant proteins is somewhat of a concern regarding the results, as it can be difficult to parse what cellular effects are due to altered protein activity versus altered protein levels, however this protein expression effect is consistent with previous literature and is likely unavoidable for this investigation. *

*Overall, the characterization of SLC25A46's localization, interactions, and effects on protein and mitochondrial structural/network organization suggests a function in mitochondrial OMM contact sites and that loss or mutation of this protein results in significant stress to the mitochondria with downstream effects. *

*Minor comments: *

*- What type of fibroblasts were used and was any subject information worth mentioning? I did not find this mentioned anywhere. *

We added an explanation in the Materials and Methods: “Fibroblasts were obtained from a cell bank located in the Montreal Children’s Hospital and the cell line we used was from a female healthy subject, 58 years old.”

*- For the confocal and STED microscopy use, what laser power was used for each excitation? More detail on the settings used for imaging with the microscopes would be help for experimental reproducibility. *

We have added to the Materials and Methods: For confocal microscopy “A laser power of 10 (for i.e. anti-PRDX3, MitoTracker, anti-OPA1) or 20% (anti-SLC25A46, SLC25A46-GFP) with a dwell time of 100 - 500 μs was used, depending on the strength of the antibody.” For the STED microscopy, we added: “A laser power of 90% was used for the confocal lasers and a laser power of 100% was used for the STED laser with dwell times of 5 μs and 20 μs, respectively.”

- Figure 7 C - the bar graph is very squished; one can barely see the levels of the small bars.

We have modified Figure 7C to make the results more visible.

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Referee #2

Evidence, reproducibility and clarity

See below my comments

Significance

The manuscript "SLC25A46 localizes to sites of mitochondrial fission and fusion and loss of function variants alter the oligomerization states of MFN2 and OPA1" partially characterizes the outer mitochondrial membrane protein SLC25A46, finding a localization to the tips and branching points of mitochondria and an effect on both mitochondrial internal structure and mitochondrial network dynamics in deletions and expression of specific mutants. The localization was conducted both with tagged protein and antibodies, which is appreciated, as tagging and overexpression can often alter localization of mitochondrial proteins. Interestingly, disease variants have an opposite effect as the deletion in mitochondria network behavior, with fragmented mitochondria in deletion strains and elongated or fused mitochondria in the mutant strains. The paper also finds alteration on membrane composition, and postulates a function in lipid exchange. While the paper falls short of a full functional characterization, the results are reasonable, internally consistent, and promising for future follow-ups.

Altered protein expression levels for the disease variant proteins is somewhat of a concern regarding the results, as it can be difficult to parse what cellular effects are due to altered protein activity versus altered protein levels, however this protein expression effect is consistent with previous literature and is likely unavoidable for this investigation.

Overall, the characterization of SLC25A46's localization, interactions, and effects on protein and mitochondrial structural/network organization suggests a function in mitochondrial OMM contact sites and that loss or mutation of this protein results in significant stress to the mitochondria with downstream effects.

Minor comments:

• What type of fibroblasts were used and was any subject information worth mentioning? I did not find this mentioned anywhere.
• For the confocal and STED microscopy use, what laser power was used for each excitation? More detail on the settings used for imaging with the microscopes would be help for experimental reproducibility.
• Figure 7 C - the bar graph is very squished; one can barely see the levels of the small bars.

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Referee #1

Evidence, reproducibility and clarity

In this MS, Scheuttpelz et al demonstrate that SLC25A46, a novel member of the mitochondrial carrier protein family localized to the outer-mitochondrial membrane, is an important regulator of mitochondrial dynamics. They show that knockout of SLC25A46 results in mitochondrial fragmentation, whereas over-expression of WT SLC25A46 or pathogenic variants/mutants of SLC25A46 results in mitochondria hyperfusion. SLC25A46 might affect fusion/fission directly since it is localized to both mitochondrial fusion and fission sites. Moreover, its loss/expression of variants alters the levels of the high molecular weight complexes of MFN2 and alters the levels of the long/short forms of OPA1. In addition, Scheuttpelz et al show that loss of SLC25A46 results in changes in the mitochondrial lipid profile, suggesting that SLC25A46 might regulate mitochondrial dynamics via regulation of mitochondrial lipid metabolism. Thus, the findings described are novel and exciting, however it remains poorly understood how SLC25A46 localization to fusion/fission sites is related to mitochondrial fusion/fission, and how are these results related to its effect on the MFN2/OPA1 complexes/forms, and to its possible role in regulating lipid metabolism.

Specific comments:

1. Are the DRP1 and the DRP1-receptor native complexes (appearing in BN-PAGE) altered in the SLC25A46 KO/+pathogenic variants cells?
2. Do the pathogenic variants of SLC25A46 localize only to mitochondria? Do they fold similar to the WT protein (i.e., similar prot K cleavage products)? Are they loss- or gain-of-function variants/mutants?
3. The BN-PAGE results presented in Fig 5 appear without molecular weight markers, and thus the sizes of the complexes are not known. Why did the authors conclude that the bands that appear in the MFN1, MFN2, and OPA1 blots represent monomers and oligomers of these proteins (Fig 5b)? Is it possible that all/part of these immune-reactive bands represent complexes with other proteins and not monomers and/or homo-oligomers? How does SLC25A46 affect the complex state of these proteins if it does not associate with them in the native state, as seen in Fig 5d?
4. Fig 5b (MFN2 blot): SLC25A46 KO cells expressing each of the pathogenic variants/mutants of SLC25A46 show different levels of the MFN2-immuoreactive higher molecular weight band (MFN2-HMWB; last three lanes), however all three cell lines show mitochondria hyperfusion. Moreover, the intensity of the MFN2-HMWB in two of these mutant lines (+T142I and +E335D) is similar to the intensity of the band that appears in the SLC25A46 KO cells, cells which show fragmented mitochondria. Thus, there is not a clear correlation between the state of SLC25A46, the levels of the MFN2-HMWB, and the mitochondrial morphology.
5. The authors' interpretations of the results presented in Fig 5d, arguing that there is a correlation between the appearances of the short/long forms of OPA1 and the fusion/fission state of the different cells, are not convincing. BN-PAGE results can vary between experiments, and thus need to be repeated and accompanied by densitometry analyses, especially in cases where the intensity of the bands (short and long forms of OPA1) seem largely similar in the single experiment presented.

Significance

See above

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Reply to the reviewers

We thank the reviewers for thorough reading and for providing useful suggestions to improve our manuscript. We find two major issues indicated by the reviewers.

1. Lack of pathophysiological relevance to attract a broader readership – to address, we have stained brain slices of PD patient’s with p129-Syn and Lamin B1 antibodies. Microscopy images show extensive lamina damages in the patient brain slices which contain p129-Syn positive inclusions. These images are now included in the current revision of the manuscript as 6C-D. We think that these results in the pathologically relevant systems will now establish a connection between lamina defects with neurodegeneration in PD and will be attractive for a broader audience.

Experimental issues as indicated by major and minor points – majority of the points have been addressed in the current revision attached herewith. Given opportunity to submit a full revision, we shall incorporate more experiments to address all the points in the final revised manuscript.

Point by point response to reviewer’s concerns:

Reviewer 1

R1: The work by Mansuri and collaborators reports that LB-like filamentous inclusions of α-Synuclein are able to associate with and perturb the nuclear lamina due to an unbalanced mechanical tension between cytoskeleton and nucleoskeleton. Consequently, lamina-injuries are proposed as a major driver of proteostasis sensitivity in cells with LB-like Syn-IBs.

It is a complex work, in which a range of different cellular, biochemical and molecular techniques have been used. Readers of the paper (including the undersigned) will be wondering if a similar behaviour occurs in pathological systems, such as iPSC derived dopaminergic neurons arising from patients carrying the synuclein pathological mutations reported in this work.

Response: We thank the reviewer for bringing out the lack of pathophysiological relevance in our manuscript. To address, we imaged post-mortem thalamus sections of a Parkinson’s Disease (PD) patient (BioChain Institute Inc., USA Cat# T2236079Par) and a control (BioChain Institute Inc., USA Cat#T2234079). Our experiments clearly show extensive lamina deformities in the patient brain (Fig. 6C-D) and connects with neurodegeneration in a pathological system.

Major points

R1: Authors should explain why there is a so high amount of p129-Syn in unseeded neurons (Fig. 1Ai, Fig. S1Bi): "p129-Syn was distributed throughout the neuron cell body and projections including light staining in the nucleus", as its accumulation is typical of PD-like α-syn aggregates. Similarly, unseeded neurons labeled with p129-Syn in Fig. 1Ai, Fig. 1Bi, and Fig. S1Bi and Fig. S1Ci are very different each other. Why? As neurons are unseeded, the pathological signature of PD-like α-syn aggregates should be very low or absent in all cases.

Response: We agree with the reviewer that very low amount of p129-Syn should be present in unseeded neurons. We standardized microscopy parameters using fields that contained neurons with both large LB-like perinuclear IBs and smaller peripheral Syn-filaments. We used Leica SP8 confocal microscope. Argon laser power was kept constant at 30% of full potential while Smart Gain was titrated to visualize the smaller filaments. For example, the smaller filaments were not clearly visible in Annexure Figure 1Ai when Smart gain was 690V. Smaller filaments were prominent when the Smart Gain was increased to 848V (Annexure Figure 1Aii, included with the revision plan attached herewith). We also observed light intra-nuclear staining of p129-Syn at 848V Smart Gain when we zoomed the arrow indicated nucleus in Fig. 1Aii shown below as Annexure Figure 1Aiii. Accordingly, we used Smart Gain: 650-850V in all the images presented in the manuscript. Brightness and contrast are now adjusted for all the images prepared for the revised manuscript for the optimum view of the immunostaining. All the raw image files will be submitted to https://www.ebi.ac.uk/biostudies in due course.

In order to rule out imaging artefacts at the higher Smart Gain (650V – 850V), we performed a control experiment without adding primary antibody against p129-Syn during immunostaining. Secondary antibodies were added and the Smart Gain was ~950-1000V during imaging. The light staining of p129-Syn as visible in Fig. 1Ai and 1Bi in the revised manuscript were not visible in this experiment (Annexure Figure 1B).

A table indicating the Smart Gain for all the images is included in the revised manuscript as__ Methods Table S5 - Laser Intensity.__

Reviewer 1 has also pointed out the difference in staining of p129-Syn in Fig. 1Ai and Fig. 1Bi. For Fig.1Ai, Rabbit monoclonal (p129-Syn (MJF-R13 (8-8), epitope: phosphoserine 129, cat# ab168381), and for Fig. 1Bi Mouse monoclonal (P-syn/81A, epitope: phosphoserine 129, cat# ab184674) were used. This information is now included in the figure legends. The difference in the staining pattern is due to the use of the different primary and secondary antibodies.

Lastly, we want to emphasize that the staining pattern seen in unseeded neurons () are not the typical PD-like Syn-aggregates but the soluble p129-Syn that is yet to be incorporated into the amyloid-filaments. p129-Syn ((antibody MJF-R13 (8-8)) staining pattern in 1Ai is continuous in the projections and light dotted in the periphery and inside nucleus. These dots also accumulate on the Microtubule Organizing Centre (MTOC) indicating the presence of aggresome-like inclusion bodies in the neurons. The staining pattern in 1Bi (antibody P-syn/81A) is dotted throughout. In both the cases, the continuous or dotted staining were not observed after seeding. The continuous staining at the projections seen in 1Ai is broken into smaller filaments in 1Aii (indicated by arrowheads). The broken filaments are much more increased in number and length in Fig 1Bii and the staining-intensity prominently increased. Accumulation of multiple larger filaments into perinuclear LBs is typical PD-like (Fig. 1Bii, yellow arrowhead).

The continuous staining and the broken staining patterns at the projections are also visible in the zoomed out MIP images presented in S1Bi and ii, respectively. The increase in fluorescence intensity of p129-Syn staining is prominent between S1Ci and ii indicating accumulation of p129-Syn in the form of large amyloid filaments in seeded neurons.

We now discuss the staining patterns in the revised manuscript. Please see pages 4-7.

R1: Authors should try to perform a more accurate quantification of the various colocalizations reported along the manuscript, i.e. by reporting the Pearson correlation coefficient or the Mander's overlap coefficient.

Response:As suggested by the reviewers, Pearson’s co-localization coefficient values have been added separately for all figured showing co-localization in Supplementary note: Colocalization figures and table.

Minor points

R1: In Fig. S1B the red fluorescent signal arising from γ-tubulin staining is not visible in the merged picture.

Response: Fig. S1B are the zoomed out MIP images of Fig. 1A. γ-Tubulin stains centrosome as tiny dots at the perinucleus in one of the z-sections of the MIP. To visualize these tiny dots in the MIP images, we have 1) optimized the brightness contrast of the MIP images and 2) provided a separate channel for γ-tubulin (arrowheads). These corrections are included in the revised version.

R1: Page 6: results of Fig. S1D-E should be explained properly (CALNEXIND and CMX-Ros staining).

Response:As suggested, we revised this part in Page 7.

R1: Fig. 2A: the indication of SNCA in western blotting is not proper, as in this experiment you evaluated the protein level, so it is better to report "α-syn";

Response:We agree with the reviewer. SNCA in western blots has been changed to α-Syn all the figures and figure legends.

R1: Fig. S2B: there is great variability in the number of SNCA(A53T)- EGFP and SNCA(DM)-EGFP cells with IBs during the course of PFF-incubation, so that authors did not reveal any significant difference. I think it is not completely correct to emphasize this data at page 9, lanes 12-13;

Response:We agree with the reviewer that the difference in number of SNCA(A53T)-EGFP and SNCA(DM)-EGFP cells with IBs was not statistically significant. Yet, we always observed aggressive biogenesis LB-like IBs in SNCA(DM)-EGFP cells. The statement in the manuscript is now corrected as per the reviewer’s suggestion (Page 9).

__R1:__Did authors reveal any cytotoxicity upon Congo Red treatment at the indicated concentrations (Fig. S2G)?

Response: Previously, Congo Red incubation was found to be non-toxic for neuronal cells even at 350 µM (PMID: 7991613). We have now performed MTT assay after Congo red treatment in our cells. The graph is now included as S2H. We did not observe any difference in cell viability even after treating the cells with the highest dose (100 µM) used in the experiment.

R1: I have concerns about the percentages reported in Fig. S2G: the percentage of cells with filaments in the absence of Congo Red is apparently too low as compared to the previously reported percentages.

Response:The reviewer is right. Number of Syn-filament containing cells varies between experiments because of ‘age’ of the recombinant amyloid seeds, different batches of seed preparation etc. We are repeating this experiment to increase the biological N. Results will be included and discussed in the final revised version

R1: Fig. S2G: I also believe that authors should report representative images of cells treated with Congo Red, in which Syn-filament biogenesis is prevented;

Response:As instructed by reviewer, the images are included in Fig. S2G.

R1: Fig. 2Eiii: The stick arrowhead seems to indicate a separate blob that is not so red: authors should consider to show separated channels and not only the merged picture (as in Fig. S3).

Response:We agree with the reviewer that the blob is not so red. We could not accommodate the separate channels in the main figure because of space constraint. Therefore, we presented the separate channels in Fig. S3A. Now we are including the stick arrowhead also at Fig. S3A.

R1:Page 10: authors should explain why they performed the LC3 staining;

Response:Previous reports indicated association of LC3B with α-Synuclein inclusions in neurons (PMID: 21412173, 31375560). Therefore, we also stained our cells with LC3 antibody. The references are now incorporated in Page 10.

R1: Why in Fig.2i, SNCA(DM) the ubiquitin signal is pink and not red?

Response:The blue of the DAPI is slightly overlapping with the ubiquitin staining at the aggresomes as these bodies are perinuclear making it appear pink. Separate channels are provided in Fig. S3E.

R1: Fig. 3, western blotting: as I previously reported, I think it would be better to write "total α-syn" instead of SNCA. Fig. 3D: is should be useful to explain properly the content of the soluble and insoluble fractions.

Response:We agree with the reviewer. SNCA in western blots has been changed to α-Syn all the figures and figure legends.

R1: Explain in the legend of Fig. 4 what is h2b tdTOMATO

Response:We thank the reviewer for pointing out the lack of information. This is now included with a reference in the revised manuscript.

Significance

R1: Overall this is interesting to read, a lot of data are presented, demonstrating a new potential phenomena that would be important to a specialized audience in the field of synuclein misfolding, aggregation and cellular toxicity.

Response: We have now included immunofluorescence images of post-mortem thalamus sections of a Parkinson’s Disease (PD) patient (BioChain Institute Inc., USA Cat# T2236079Par) and a control (BioChain Institute Inc., USA Cat#T2234079). Our experiments clearly show lamina deformities in patient brain (Fig. 6D). We think that these experiments will highlight the pathophysiological relevance of the manuscript to make it appropriate for a wider audience.

Reviewer 2

__R2:__The present paper titled "Nuclear-injuries by aberrant dynein-forces defeat proteostatic purposes of Lewy Body-like Inclusions" provides an in details and compelling study about the formation of aggregates of SNCA in presence of PFFs, which other proteins play a role in the formation of this inclusions, and which pathways are the major players. They study provides many well-done experiments to highlight the composition and the process formation of these aggregates. unfortunately I think the study is lacking in connecting these events with neurodegeneration. how do all the pathways study impact viability and functionality of neurons and other disease relevant cells like astrocytes and microglia? it is thus a work which mainly focuses on the pathways leading to the formation of inclusions leaving untouched the question of how this might impact the disease. This does not take away the value of the findings but it should be taken in consideration when deciding which journal to submit.

Response:We thank the reviewer for the encouraging words and also for bringing out the lack of pathophysiological relevance in our manuscript. To address, we have performed immunofluorescence experiments with post-mortem thalamus sections of a Parkinson’s Disease (PD) patient (BioChain Institute Inc., USA Cat# T2236079Par) and a control (BioChain Institute Inc., USA Cat#T2234079). Our results show extensive lamina deformities in patient brain (Fig. 6C-D) connecting neurodegeneration in PD with lamina injuries.

Further, although we found that LB-containing primary neurons and Hek293T cells do not show any loss in cell viability as estimated by LDH and MTT assays respectively (Fig 4A-B), they show sensitivity to additional stresses. LB-like IB containing Hek293T cells were unable to trigger stress response pathways and were vulnerable to heat stress. These results were already included in the earlier version of the manuscript (Fig. 4H-I). We now estimated sensitivity of neurons in presence of additional stress. We have subjected LB-containing neurons and control neurons to heat stress and estimated induction of Hsp chaperones by western blot and quantitative mass spectrometry. Preliminary results (included herewith) indicate that Hsp-upregulation is defective in neurons with LB-like IBs. These results are now included as Figure 4J-M in the attached revised manuscript. Repeat experiments with quantitative mass spectrometry will be included in the final revision.

R2: I have a few suggestion for each figure which will not take much time, energies or expenses but that would overall make the paper easier to read and digest.

R2::Fig 1: quantification of aggregates dimension, number and colocalization score with p62 (Pearson)

Response:Co-localization score with p62 is included in the current revision (Supplementary note: Colocalization figures and table). Quantification of aggregate dimension, number etc. in neurons have been already documented by Mahul-Mellier et al. (PMID: 32075919). We are following the same protocol and therefore did not repeat the counting for neurons. However, if the reviewer thinks that its mandatory, we shall do that and include with full revision.

__R2:__Fig 2: aesthetic comment: the way to read the figure should be consistent throughout the figure. they should be assembled either all in vertical or all in horizontal.

Response:We tried. We find the current organization is the best fit to accommodate all panels.

R2: Fig 3: 3E better to put an image without nocodazole to visualize the difference

Response:The control image is now added in Fig. 3E.

R2: 3D probe WB also for SNCA

Response:Sorry for the confusion. The western blots in 3D are probed for both total Synuclein and p129-Syn. As suggested by the first reviewer, we have also changed SNCA to α-Syn which indicates the total Synuclein protein level.

R2: 3K this WB needs quantification to backup the statement made

Response:We are repeating this experiment. Results will be included and discussed in the final revised version.

R2: 3I check the - and + for PFF and doxy. I believe they are wrong

Response:We have rearranged the figure. The scheme in Fig. 3I (now Fig. 3H) is correct but we have made it simpler to avoid confusion.

R2: Fig 4: missing IF of peri nuclear IBs with HS

Response:The images are now included as Fig. S4E and discussed in page 19.

R2: Fig 5: quantification of H2BTdTom exit from the nucleus

Response:We have performed this experiment as a supporting evidence of the nuclear damage in presence of LB-like IBs. We have quantified the damages in Fig. 5A and D. We have also performed quantitative mass spectrometry to show nuclear entry of associated organelle proteins (Fig. S5G). We think, quantifying the H2BTdTom exit will not be a significant value addition to the manuscript.

R2: Fig 6: some neurons with large PFF seems very unhealthy. is it possible to quantify neuronal viability may not with MTT which is not suited for single cells analysis?

Response:The reviewer correctly pointed out that neurons with large LB-like IBs seemed unhealthy which was confirmed by ƴH2AX staining indicative of extensive DNA damage in Fig. 6B.

R2: maybe it would be nice to have a WB with soluble and insoluble SNCA and p129 with ciliobrevin D with and without PFF. Ciliobrevin D might also impact degradative systems as demonstrated by the EHNA compound (PMCID: PMC5584856).

Response:We have performed the dynein experiments to figure out the role of cytoskeleton-nucleoskeleton tension in the lamina injuries in LB-like inclusion containing cells. However, we think that the reviewer has correctly pointed out that dynein may have a direct role in degrading Synuclein by either autophagy or proteasome. Given the results of the suggested experiments are not going to change the final conclusion of the manuscript, we propose to limit ourselves in discussing this possibility and citing the paper in the current revised version of the manuscript (page 29).

Significance

R2: As already stated above, the experiments are correctly performed and the evidence are well-presented and demonstrated. the realm that this paper falls into is not though neuroscience. The aim of this paper is to study the formation of inclusions regardless of their impact on disease-relevant cell type functions. the presented experiments are numerous and even though the message is pretty clear some figure might be too crowded to correctly convey the message (see fig 3). some of these findings even tough with much less details were already suggested by other papers (PMCID: PMC5584856) in which the importance of the dynein was studied in the context of the communication between autophagy and proteasome. I think adding this angle with few experiments might add a little bit more relevance but it is also true that this paper has already a lot of data.

Response:Thank you very much for the encouraging comments

R2: the type of audience for this paper I think is a very specialized audience which is interested in molecular mechanisms of inclusions formation and protein-protein interaction. as a final statement the paper is beautifully done and is relevant but it lacks the translational angle.

Response:We again thank the reviewer for reminding the lack of pathophysiological relevance. We have now included microscopic images of brain slices of PD patients with extensive lamina defects (Fig. 6D) and think this will attract a broader audience.

R2: my field of expertise is neuroscience. I have expertise in bimolecular techniques as well as cellular techniques to study neurodegenerative diseases

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Referee #2

Evidence, reproducibility and clarity

The present paper titled "Nuclear-injuries by aberrant dynein-forces defeat proteostatic purposes of Lewy Body-like Inclusions" provides an in details and compelling study about the formation of aggregates of SNCA in presence of PFFs, which other proteins play a role in the formation of this inclusions, and which pathways are the major players. They study provides many well-done experiments to highlight the composition and the process formation of these aggregates. unfortunately I think the study is lacking in connecting these events with neurodegeneration. how do all the pathways study impact viability and functionality of neurons and other disease relevant cells like astrocytes and microglia? it is thus a work which mainly focuses on the pathways leading to the formation of inclusions leaving untouched the question of how this might impact the disease. This does not take away the value of the findings but it should be taken in consideration when deciding which journal to submit.

I have a few suggestion for each figure which will not take much time, energies or expenses but that would overall make the paper easier to read and digest.

Fig 1: quantification of aggregates dimension, number and colocalization score with p62 (Pearson)

Fig 2: aesthetic comment: the way to read the figure should be consistent throughout the figure. they should be assembled either all in vertical or all in horizontal.

Fig 3: 3E better to put an image without nocodazole to visualize the difference 3D probe WB also for SNCA 3K this WB needs quantification to backup the statement made 3I check the - and + for PFF and doxy. I believe they are wrong

Fig 4:missing IF of peri nuclear IBs with HS

Fig 5: quantification of H2BTdTom exit from the nucleus

Fig 6: some neurons with large PFF seems very unhealthy. is it possible to quantify neuronal viability may not with MTT which is not suited for single cells analysis

Fig 7: maybe it would be nice to have a WB with soluble and insoluble SNCA and p129 with ciliobrevin D with and without PFF. Ciliobrevin D might also impact degradative systems as demonstrated by the EHNA compound (PMCID: PMC5584856).

Significance

As already stated above, the experiments are correctly performed and the evidence are well-presented and demonstrated. the realm that this paper falls into is not though neuroscience. The aim of this paper is to study the formation of inclusions regardless of their impact on disease-relevant cell type functions. the presented experiments are numerous and even though the message is pretty clear some figure might be too crowded to correctly convey the message (see fig 3). some of these findings even tough with much less details were already suggested by other papers (PMCID: PMC5584856) in which the importance of the dynein was studied in the context of the communication between autophagy and proteasome. I think adding this angle with few experiments might add a little bit more relevance but it is also true that this paper has already a lot of data.

the type of audience for this paper I think is a very specialized audience which is interested in molecular mechanisms of inclusions formation and protein-protein interaction. as a final statement the paper is beautifully done and is relevant but it lacks the translational angle.

my field of expertise is neuroscience. I have expertise in bimolecular techniques as well as cellular techniques to study neurodegenerative diseases

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Referee #1

Evidence, reproducibility and clarity

The work by Mansuri and collaborators reports that LB-like filamentous inclusions of α-Synuclein are able to associate with and perturb the nuclear lamina due to an unbalanced mechanical tension between cytoskeleton and nucleoskeleton. Consequently, lamina-injuries are proposed as a major driver of proteostasis sensitivity in cells with LB-like Syn-IBs. It is a complex work, in which a range of different cellular, biochemical and molecular techniques have been used. Readers of the paper (including the undersigned) will be wondering if a similar behaviour occurs in pathological systems, such as iPSC derived dopaminergic neurons arising from patients carrying the synuclein pathological mutations reported in thins work.

There are some concerns that should be addressed by the authors.

Major points

• Authors should explain why there is a so high amount of p129-Syn in unseeded neurons (Fig. 1Ai, Fig. S1Bi): "p129-Syn was distributed throughout the neuron cell body and projections including light staining in the nucleus", as its accumulation is typical of PD-like α-syn aggregates. Similarly, unseeded neurons labelled with p129-Syn in Fig. 1Ai, Fig. 1Bi, and Fig. S1Bi and Fig. S1Ci are very different each other. Why? As neurons are unseeded, the pathological signature of PD-like α-syn aggregates should be very low or absent in all cases.
• Authors should try to perform a more accurate quantification of the various colocalizations reported along the manuscript, i.e. by reporting the Pearson correlation coefficient or the Mander's overlap coefficient. Minor points
• In Fig. S1B the red fluorescent signal arising from γ-tubulin staining is not visible in the merged picture.
• Page 6: results of Fig. S1D-E should be explained properly (CALNEXIND and CMX-Ros staining).
• Fig. 2A: the indication of SNCA in western blotting is not proper, as in this experiment you evaluated the protein level, so it is better to report "α-syn";
• Fig. S2B: there is a great variability in the number of SNCA(A53T)- EGFP and SNCA(DM)-EGFP cells with IBs during the course of PFF-incubation, so that authors did not reveal any significant difference. I think it is not completely correct to emphasize this data at page 9, lanes 12-13;
• Did authors reveal any cytotoxicity upon Congo Red treatment at the indicated concentrations (Fig. S2G)?
• I have concerns about the percentages reported in Fig. S2G: the percentage of cells with filaments in the absence of Congo Red is apparently too low as compared to the previously reported percentages.
• Fig. S2G: I also believe that authors should report representative images of cells treated with Congo Red, in which Syn-filament biogenesis is prevented;
• Fig. 2Eiii: The stick arrowhead seems to indicate a separate blob that is not so red: authors should consider to show separated channels and not only the merged picture (as in Fig. S3).
• Page 10: authors should explain why they performed the LC3 staining;
• Why in Fig.2i, SNCA(DM) the ubiquitin signal is pink and not red?
• Fig. 3, western blotting: as I previously reported, I think it would be better to write "total α-syn" instead of SNCA.
• Fig. 3D: is should be useful to explain properly the content of the soluble and insoluble fractions.
• Explain in the legend of Fig. 4 what is h2b tdTOMATO.

Significance

Overall this is interesting to read, a lot of data are presented, demonstrating a new potential phenomena that would be important to a specialized audience in the field of synuclein misfolding, aggregation and cellular toxicity.

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

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Referee #3

Evidence, reproducibility and clarity

see the "Significance" section.

Significance

This manuscript reports the role and mechanism for AF10 in inhibition of mouse somatic cell reprogramming. It is known that DOT1L inhibits somatic cell reprogramming. In this study, a number of known DOT1L-interacting proteins were examined for their role in this process. They found that only AF10 (MLLT10) plays a similar role in somatic reprogramming, i.e., deletion of AF10 promotes reprogramming of somatic cells into iPS cells. Experiments in combination with DOT1L inhibitors showed that AF10 functioned in the same pathway as DOT1L. Reprogramming with AF10 mutants revealed that the AF10-DOT1L interaction but not the binding of AF10 to unmodified H3K27 is critical for reprogramming and somatic cell identity. ChIP-seq showed that AF10 deletion caused an ESC-like pattern of H3K79me1 at house-keeping genes. The data supported the conclusions. It is well-written. This study provided mechanistic insights into the role of DOT1L-AF10 in maintaining somatic cell identity and inhibiting somatic cell reprogramming.

Major:

This study is very similar to the following publication as cited:

Deniz Uğurlu-Çimen, Deniz Odluyurt, Kenan Sevinç, Nazlı Ezgi Özkan-Küçük, Burcu Özçimen, Deniz Demirtaş, Eray Enüstün, Can Aztekin, Martin Philpott, Udo Oppermann, Nurhan Özlü, Tamer T. Önder. (2021). AF10 (MLLT10) prevents somatic cell reprogramming through regulation of DOT1L-mediated H3K79 methylation. Epigenetics Chromatin 14, 32. https://doi.org/10.1186/s13072-021-00406-7.

Both manuscripts were deposited in BioRxiv in December 2020. Clearly these were two independent studies. The methodology and conclusions are very similar.

Minor:

Fig. 1B. The Axis labels are too small.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors investigated the role of AF10, a subunit of DOT1L histone-methyl transferase complex for writing H3K79me1-2-3 marks, in cellular reprogramming. Using siRNA-mediated knockdown and chemical inhibitors, the authors show that AF10, and DOT1L as a whole, are inhibitory to reprogramming of mouse embryonic fibroblast cells (MEF) to induced pluripotent cells (iPSC), suggesting that AF10 plays an important role in determination and changes in cell lineages. The authors also show that this effect of AF10 is not transcription mediated. Based on their ChIP experiments of H3K79me1,2,3 and RNA Pol II, the authors claim that the effect of AF10 is mediated by "changes in epigenome circuitry".

Major comments

1. The claim that AF10 and DOT1L inhibits reprogramming of MEF to iPSC is largely supported by authors' experiments. Mostly, the authors used expression levels of NANOG as a mark for pluripotency. While it is a well-documented mark, an orthogonal mark (such as colony morphology, embroid bodies, etc.) will increase the rigor and confidence. This is especially important in the context of testing something like DOT1L complex which plays important role in transcription.
2. The data presented here largely supports the claim that AF10-mediated effect is not through transcription.
3. The authors final model ¬- "negative feedback by RNA-PolII recruited DOT1L leading to ESC-like state" - is not supported by the data presented here.
   • For example, at line 295, the authors say that H3K79me1 pattern in ΔAF10 "resembles the H3K79me1 found in ESCs which are much more TSS-enriched for this modification compared to MEFs." However, the data in 5H show that the pattern in ESC matches more with AF10 fl than ΔAF10.
   • At line, 299, "given that AF10 deleted cells retain H3K79 methylation..". This statement highly contradicts data in 4B, 4C, 5G and 5H where it is shown that deletion of AF10 leads to substantial loss of H3K79me1,2.
   • While the authors showed there are changes in H3K79 methylation pattern upon AF10 deletion, its link to changes in iPSC reprogramming is not shown. The Pol II occupancy data, shown for WT MEFs and ESC, do not support any of part of this claim. Even further, there is no evidence for changes in Pol II occupancy levels upon AF10 deletion.
4. How do authors reconcile that there is increased expression of AF10 in pluripotent cells (Fig. 1A and 1B) although it inhibits pluripotency?
5. Line 341, "We do not find any evidence that H3K79me2 opposes spreading of H3K27me3 in reprogramming to iPSCs" seems to be an over-interpretation. The experiment just shows that inhibition of PRC does not change global H3K79me2 levels. A direct role of H3K79me2 on H3K27me3 is not tested here.
6. Fig S1D shows that deletion of AF10 can have additional effect to inhibition of DOT1L. This is in contrast to most of the main figures, especially, fig 1E. Some comment about this discrepancy is warranted.

Minor comments

1. It might help the reader if authors put a schematic of reprogramming regimen for Fig. 1A.
2. At line 146, the authors inference " ΔAF10 is estimated to contribute about 40% of the DOT1Li phenotype in reprogramming" is not clear. It may help the reader the reader if more information is provided for their analyses and interpretation.
3. Line 324, a typo: it should be "AF10"
4. Line 456, It might be better for readers if the authors report whether and how RT-qPCR was normalized to housekeeping genes etc.
5. Line 582, It is not clear at what step human cells were spike in. Also the type of human cells should also be reported.
6. At many places (e.g. Fig 1E, Fig S3D) authors seem to have used multiple t-tests. Please consider using something like ANOVA to avoid multiple t-test error.
7. Fig 1E. It is commendable that authors show factor independent reprogramming. It will be helpful for readers if authors show number of days for OSKM-dependent and OSKM-independent growth in the schematic.
8. Fig S1C is not clear as such. Please add more information in the figure or legends.

Referees cross-commenting

With regards to reviewer1's comments: I particularly agree with major points 1 and 2 that authors' current model regarding feedback regulation needs more evidence. The technical concerns regarding ChIP normalization, esp. point 5, are also well-warranted.

With regards to rev3's comments: The major concern about another similar study is well-warranted. The authors may want to explicate compare and contrast their key inferences with the other study.

Significance

The present work provides good evidence that AF10-mediated H3K79me can contribute to cellular reprogramming independent of steady-state mRNA levels. However, I think that the manuscript falls short of providing the basis for it. The claim that it is through subtle changes in H3K79me patterns seems nebulous and unsupported by the data presented here. If the manuscript finds the mechanistic basis for AF10's role in cellular reprogramming, it will be of interest to readers in general epigenetics as well as clinical fields that use histone methyl transferase inhibitors for treating leukemia.

I am not an expert in the field of cellular reprogramming; so, I may not be able to judge the merits or caveats of authors' reprogramming methods and analyses.

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Referee #1

Evidence, reproducibility and clarity

Summary

Inactivation of the histone methyltransferase DOT1L increases the efficiency of reprogramming somatic cells to included pluripotent stem cells. Recent studies have shown that loss of the DOT1L-interacting protein AF10 or disruption of the DOT1L-interacting domain (OMLZ) of AF10 phenocopies DOT1L inhibition in human cells. Here, Wille et al use a transgenic reprogrammable mouse model to study the role of AF10 in reprogramming of mouse somatic cells. Using a conditional AF10 deletion allele, loss of AF10 was found to partially phenocopy inhibition of DOT1L and evidence is provided that AF10 and DOT1L act in the same pathway. Elegant rescue experiments showed that loss the OMLZ domain is sufficient to abolish the programming-barrier function of AF10. In contrast to human cells, AF10 deletion had a minimal impact on mRNA expression during reprogramming. Analysis of H3K79me1/2 patterns showed that AF10 loss leads reduced H3K79me1/2 levels across the genome, and a redistribution of H3K79me1 at highly expressed genes from a peak in gene bodies to a peak downstream of the TSS. This pattern is similar to that seen in ESCs, in which DOT1L activity and overall methylation levels are lower compared to MEFs. These findings provide evidence for the model that the DOT1L-AF10 interaction is critical for efficient H3K79 methylation and for posing a reprogramming barrier. In the absence of AF10, DOT1L can still methylate histones at highly expressed genes, presumably due to interactions with RNA Pol II and transcription elongation factors, but its overall activity is reduced.

Major points

1. The quantitative ChIP-seq analyses of H3K79me1 and H3K79me2 in control and AF10 knock-out cells reveal interesting patterns. In MEFs, H3K79me2 peaks at TSSs and H3K79me1 more in gene bodies, consistent with high DOT1L activity and conversion of H3K79me1 to H3K79me2 at TSSs. In ESCs, in which the nuclear DOT1L activity is much lower, H3K79me2 levels at the TSS are lower and H3KK79me1 levels at the TSS higher. AF10 loss during programming leads to a pattern similar to that found in ESCs. The authors suggest that 'deletion of AF10 is likely to enhance reprogramming by making the epigenome more ESC-like at predominantly housekeeping genes' (and Fig 6). This is an interesting hypothesis. However, the data is also consistent with an alternative and more-simple model that AF10 is needed to boost the catalytic activity of DOT1L and that partial loss of DOT1L activity upon loss of Af10 is sufficient to promote reprogramming. The latter model is supported by the observation that DOT1Li has dose-dependent effects and that loss of AF10 enhances reprogramming in combination with a range of DOT1Li concentrations and thus at a range of H3K79me1/2 levels (Figure S1). It would be useful to discuss different models side by side.
2. In this context, the role of housekeeping genes also deserves attention. Line 276: 'Thus, the effect of AF10 deletion on promoting pluripotency occurs on genes that are commonly H3K79 methylated across cell types and not at specific lineage genes'. There is indeed a difference between highly and more lowly expressed genes but the causal relationship and role of housekeeping genes require further study. The data presented in this paper do not demonstrate that AF10 deletion affects pluripotency via genes that are commonly methylated by DOT1L. Therefore, without additional data, it seems too early to propose models of transcriptional feedback for biosynthetic/housekeeping genes (Discussion).
3. For the ChIP-seq studies, a spike-in method is used to detect and take into account global differences in histone methylation. This method is based on the ChIP-Rx protocol of Orlando et al (2014). In the Orlando study, Drosophila chromatin was used for spike with the rationale that there is little homology between human/mouse and fly genome sequence, leading to minimal mapping of spike-in fly genome reads to the human/mouse genome. Here, the authors use mouse chromatin with a human chromatin spike-in. In the analysis method described (first mapping to the mouse genome and then aligning unmapped reads to the human genome), this potentially leads to mapping of human spike-in reads to the mouse genome. Even though the human spike in is only 1/53th of the total sample, the authors should adjust their ChIP analysis to avoid this issue. One possible solution is to generate a combined human-mouse reference genome, map unique reads, and then calculate the fraction of reads mapped to human and mouse. Alternatively, non-unique regions can be blacklisted.
4. Related to the previous point, it is not clear to me how the scaling factor is calculated based on the numbers of Table. 1. The numbers given for the scaling factors do not seem to relate to the ratio of mouse/human reads. The authors should explain the scaling factor in more detail.
5. H3K79me enrichment is calculated per gene body, normalized per kilobase of gene length. The authors should consider alternative metrics. While the method used is suitable for histone modifications that occur across the gene body, it might be less suitable or relevant for H3K79me, which predominantly occurs at the 5' end of transcribed gene bodies until it reaches internal exons (DOI 10.1038/nsmb.1924). Based on this distribution, normalizing per kilobase of gene length will lead to artificial lower enrichment scores for longer genes. Given the predominant localization of H3K79me at the 5' end of genes bodies, it seems more meaningful to calculate H3K79me enrichment in this region only instead of normalize per gene length.
6. The label of Figure 1B is hard to read and the cell dots are hard to distinguish. Please increase font size and resolution. In this panel it is not clear to me whether the color indicates (graded) expression level or a more binary detection of transcripts? If the latter is the case, the signal (detection of a transcript in a single cell) might depend on the expression level of a transcript and the sequencing depth of each sample. Because of this uncertainty, it seems premature to speculate, based on single cell RNA-seq data, about variation in DOT1L complex formation. The authors should discuss this and take this into account in the analysis and representation of the data, or remove the panel and panel S1A.
7. Several figure panels have very small fonts. Some of the text is not readable. The authors should increase the font size of these panels. Some of the legends are incomplete. Please explain all the abbreviations used in the legends.

Minor points

Figure 1D. Please explain the abbreviations in the legend.

Figure 1E and 3F. Please explain the statistical test in the legend: e.g. tested against ff control. If the data was normalized to deltaAF10+DOT1Li, how was this condition taken along in the statistical test?

Figure 1F. The line can be drawn this way across the datapoints but whether or not this is evidence for a linear relationship is not clear because the data points do not all follow the trend. More importantly, the added value of this analysis is not obvious. Clearly, a higher fraction of Af10-deleted cells is expected to lead to a higher fraction of cells with a programming phenotype associated with Af10 loss. I suggest that this panel is removed but that the relevant notion that near complete of Af10 loss contributes about 40% of the DOT1Li phenotype is maintained.

Figure 3B/D. The pairing of the figure panels can lead to confusion. Empty vector refers to fl cells (black bar) as well as deltaAF10 cells (set to 100% and used as a reference; please add a dashed line at 100% with deltaAF10 label like in Fig. S3B), while the other constructs refer to deltaAF10 cells. To avoid confusion it would help to separate panel B and D and in panel D more clearly separate the fl cells from the deltaAF10 cells.

Figure 3-4. Tubulin is used as a loading control for H3K79me1/2. A pan-histone H3 would be a more unambiguous control.

Figure 4D. This panel shows changes in H3K79me1/2 ChIP-seq in DOT1Li treated vs control. Was this data normalized by the spike-in method? The samples are not mentioned in Table 1. The same question applies to the ESC vs MEF comparison.

Figure 5B. It is not clear to what section of the bars the percentages next to the bars refer to.

Figure 5D. Overlap of gene should be overlap of genes

Figure 5G-H. Please explain the percentages in the legend.

Figure S1B. Please explain the error bars and number of replicates.

Figure S1D. The error bars refer to technical replicates. The authors should show biological replicates.

Figure S2B. I could find a discussion in the text of the enriched motif of Cluster 7.

Figure S3A. The axis labels are not readable. Please explain the two axes and the rationale for using this gate.

Figure S3B. The authors should use SD instead of SEM.

Significance

This study builds on a growing body of work on the role of DOT1L in reprogramming of somatic cells. Recent studies point to a connection with the DOT1L-binding protein AF10 but the mechanisms, especially at the level of the epigenome, remained unclear. In general, very little is known about how DOT1L, its partners, and the methylation it deposits affect gene expression and cell fate.

This study confirms that in mouse cells, similar to human cells, the DOT1L-interaction domain is involved in the reprogramming function of AF10. Importantly, in contrast to human cells, in the mouse model AF10 loss has minimal effect on gene expression, suggesting that alternative mechanisms must be involved. Focusing on the epigenome, and using a quantitative ChIP approach, the authors describe how H3K79me1 and H3K79me2 are affected by loss of AF10 and how this relates to gene expression and occupancy of RNA PolII. Although the precise mechanisms remain to be elucidated, the results provide an important basis for identifying the relevant molecular changes at the epigenome.

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Reply to the reviewers

Manuscript number: RC-2022-01682

Corresponding author(s): Peter Keyel

1. General Statements

We thank the reviewers for their thorough and critical analysis of our manuscript. We have addressed most of the concerns and questions with our revised version. To address the remaining concerns, we plan to perform two lines of experiments— aerolysin sensitivity of dysferlin null C2C12 muscle cells and aerolysin sensitivity of ESCRT-impaired cells. When these experiments are complete, we believe the revised contribution will provides important novel insights into membrane repair that will appeal to a broad audience.

Reviewer comments below are in italics.

Description of the planned revisions

Reviewer 1

Major

In order to show that patch repair is indeed protecting cells against aerolysin, the authors should disrupt patch repair of the cells under study and observe and increased toxicity.

Reviewer 2

Major

*1. The effect of dysferlin overexpression does not indicate that patch repair is a protective mechanism or that dysferlin plays a significant role in aerolysin resistance. The authors should knock out dysferlin and assess cell resistance to lysis. *

Reviewer 3

Significance

The work presents a foundation to further investigate into the mechanism of aerolysin function, following the discovery of the role of extracellular Ca2+ in its activity. As aforementioned, the role of dysferlin in resisting aerolysin also has potential, but the limitations of this work were discussed including the absence of performing a dysferlin knockout, although performing this experiment may help to strengthen the current finding.

We agree with all 3 reviewers that a dysferlin knockout will complement our gain-of-function studies and this will strengthen the manuscript. We plan to challenge C2C12 myocytes that express control shRNA or dysferlin shRNA with toxin and determine their sensitivity.

We chose this system instead of targeting a patch repair protein in HeLa cells for 3 reasons. First, it will provide the corresponding loss-of-function experiment to match the gain-of-function experiments we have already done. Second, other patch repair proteins work redundantly with other proteins, complicating their knockdown and/or their disruption may interfere with lipid/protein transport. Finally, dysferlin null C2C12 cells are commercially available, so other groups will have an easier time replicating our results.

Reviewer 1

Significance

*and in the statement that a cellular process that has been artificially introduced in the experimental system is the cellular protection mechanism against aerolysin attack. In order to prove that this process is a bona fide protection mechanism, the authors should show that it is present without the need of overexpressing a protein that is not expressed at all either in the used cell line (HeLa), or in the natural cellular target of aerolysin (epithelial cells). The significance of the proposed protection mechanism is therefore questionable. *

We plan to address this concern by using C2C12 muscle cells that have and do not have dysferlin. Muscle cells are natural cellular targets of Aeromonas during necrotizing soft-tissue infections.

Reviewer 2

Major

*2. ESCRT complex was shown to play a role in plasma membrane repair following mechanical damage or perforin treatment of cells (Jimenez 2014, and Ritter, 2022). Whether ESCRT is important in aerolysin pore repair can be assessed by knocking out the Chmp4b gene or overexpressing dominant-negative mutant of VPS4a, E228Q. *

We plan to use a previously characterized (Lin 2005 PMID: 15632132) inducible system (TRex cells) to express the dominant negative VPS4b E235Q in cells. We plan to pulse cells for 2 h with 1 ug/mL doxycycline one day prior to the assay. This pulse time and dose strikes a balance between cell death due to non-functional ESCRT, and compromising ESCRT function. Then we will challenge parental cells (TRex) or TRex cells expressing VPS4b E235Q with toxin and measure lysis. We also plan to compare plus/minus doxycycline as a further control. We will also use fluorescent toxins to compare binding across cell types.

One caveat on the ESCRT work is that ESCRT has an essential role in MVB formation, and ESCRT effects might be due to perturbation of protein/lipid flux through this system in addition to their recruitment to the plasma membrane. Even with knockdowns and overexpression, it can be challenging to interpret some of the pleiotropic effects of altering the ESCRT complex. While we do not contest the role for ESCRT in plasma membrane repair, we suspect the role for ESCRT will be more complicated than previously appreciated. Digging deeper into these possibilities beyond our proposed experiment is beyond the scope of this manuscript.

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

Reviewer 1

*Major: The authors conclusions contradict established results, which they cite. Yet experimental conditions are not similar in two ways: toxin concentration-wise and toxin treatment duration-wise. *

We agree with the reviewer that there were differences in experimental design between our study and the other cited studies. Due to the cited differences, our results, Gonzalez et al and Larpin et al are not necessarily contradictory on most points. Our conclusions differ from Gonzalez et al in that we do not think K+ efflux drives repair in the first hour, and differ from Larpin et al in that we observe Ca2+ flux after aerolysin challenge. Along with the toxin variables discussed below, we also discussed the potential cell type differences between the studies that may account for the discrepancy. We have now included these additional differences in our manuscript on line 435 for Larpin et al and lines 423-425 for Gonzalez.

Our study set out to do something distinct from the prior studies. The prior studies did not compare the efficacy of distinct membrane repair mechanisms to the same toxin because that was not their study aim. Hence, our goal is not to prove the prior literature wrong, but contribute to a better understanding of the immediate membrane repair events triggered by aerolysin. We argue that the significance of our contribution is this comparative approach to membrane repair, which has not previously been done, and our finding that aerolysin engages distinct, but overlapping mechanisms compared to CDCs. We have updated our significance to better convey our advance, which is explained on lines 99-102, 128, 519-525.

*While we appreciate the efforts of the authors to standardize the concentration of toxins used based on hemolytic units, we note that the concentrations used are very much higher than in the other studies cited. Indeed, based on table 1, materials and methods, and the various experiments, aerolysin has a LC50 of approximately 200 HU/ml, which corresponds to about 2 ug/ml. This is approximately 200x more concentrated than for example in Gonzalez et al 2011 and Larpin et al. 2021. It makes the validity of direct comparison with those studies questionable. *

We agree with the reviewer that the toxin concentrations are different from prior studies. This is why we argue hemolytic activity needs to be reported along with toxin mass.

One potential explanation for this difference is purification method. We do nickel NTA purification from whole bacterial lysates, instead of from the periplasm. It is possible that the most active aerolysin precipitates early or is otherwise lost in our purification process, which accounts for both the lower toxin specific activity and lack of toxin precipitation during trypsin activation that we observe. To control for impurities, we purified two preps of our aerolysin to >90% purity after nickel beads. However, we did not observe a significant change in specific activity or cytotoxic activity. We interpret this finding to suggest there was a trade-off between improved specific activity due to increased purity and loss of specific activity due to toxin inactivation during the extended purification process.

We have included a new figure (Fig S10) showing our toxin purification and activity.

*We noticed that the authors activate pro-aerolysin at high concentration (in the range of 1 to 5 mg/ml) and at room temperature. In our experience, under these concentration, activation leads to immediate oligomerization and massive precipitation. The final concentration of active toxin is thus unknown. *

When we titrated the trypsin to determine the optimal concentration of trypsin to use, we did not observe oligomerization/precipitation (Fig S10B). If there was precipitation of aerolysin after trypsin treatment, we would expect a difference in cytotoxicity between pro-aerolysin and aerolysin treatment. We did not observe significant differences in cytotoxicity between pro-aerolysin and activated aerolysin (see Figs 1-2). Finally, we measured hemolytic activity on trypsin-activated toxin, so any precipitation would be expected to occur prior to assessing hemolytic activity. Thus, we argue our use of hemolytic activity measured after trypsin activation mitigates this risk.

* The authors keep their cells in toxin-containing medium for the whole duration of the experiments, typically 45 minutes. This is in stark contrast with 45 seconds to 3 minutes transient exposure to toxin in Huffman et al 2004. *

We agree this is one of the differences. We also note Huffman et al examined cells at 6 or 28 h later. While we ruled out the impact of MAP kinases on membrane repair occurring within 30 min of toxin challenge, we make no claims about their ability to promote cell survival at later time points. We have clarified these differences in the manuscript (line 461).*

The authors do not report binding and oligomerization assays of the toxins. The only figure showing a western blot (fig. 7) is of low quality and shows unexpected observations. Aerolysin Y221G mutant is expected to bind and oligomerize. Yet, no band is present at about 250 kDa (expected oligomer) or at about 47 kDa (monomer). In addition, in aerolysin lanes (1 and 2) the oligomer is saturated, seems to be covering three lanes, indicating a possible spill-over. *

We performed binding studies in Fig S3C and Fig S5. For Fig 7, in the original blot, the cell lysate is a wider band than the MV band, but there are only two bands, that remained in their respective lanes. We have now included another independent biological replicate of the aerolysin blot as Supplementary Fig S7D which shows clear demarcation between cell lysate and MV pellet. This blot was not included in the main figure because in the process of stripping and reprobing for all of the targets, we lost detection of our penultimate targets. We agree with the reviewer that oligomer bands for the Y221G were very faint, and we expected them to be stronger. In the new blot (Fig S7D), some oligomer can be detected. As a result, we are hesitant to risk over-interpreting these findings.*

Finally, while the patch repair hypothesis is interesting, it is unclear why the authors decided to overexpress dysferlin in cell lines that normally do not express it. Sure, there is a repair phenotype but this phenotype is artificially introduced. Dysferlin is not expressed at all in HeLa cells. *

One challenge with membrane repair is the difficulty perturbing the system due to redundancies. While loss-of-function experiments are important, gain-of-function experiments also add confidence to the system. The simplest way to perform a gain-of-function experiment is to add a well-known patch repair protein to a well-characterized cell line lacking it. Thus, exogenous expression of dysferlin enables us to test the hypothesis that increasing patch repair enhances repair against the toxins.

We have included this rationale now in the manuscript, lines 366-369

*Furthermore, dysferlin is not expressed in epithelial cells, which are the prime target of aerolysin. Why then focus on this protein? *

We chose dysferlin because it is well-characterized as a patch repair protein, whose defect causes Limb-Girdle Muscular Dystrophy 2B and Miyoshi Myopathy. Additionally, setting up this assay enables future work to probe the role of individual dysferlin domains in patch repair.*

Minor: The graphic legends should be boxed out to be clearly separated from the data. In Figure 4A, it is mixed up with the data. *

This has been corrected.*

Some western blots are saturated, e.g. B-actin in figure 4B. Full blots should be provided. *

We have added full western blots as requested as Supplementary Figs S11-12.*

In the methods, aerolysin sublytic dose for HeLa cells is specified at 62 HU/ml. In figure 5C and D, 31 HU/ml kills more than 50% of HeLa cells. This is not compatible. *

Even when controlling by hemolytic activity, and toxin prep, we find some variability in toxin activity between assays. For the live cell experiments, 62 HU/mL remained sublytic despite the higher activity in the flow cytometry assays. We controlled for death in our live cell imaging experiments, by including TO-PRO. This confirmed the toxin was at a sublytic dose in those experiments.

We included a new figure S10C to show the variation in LC50 per assay as a function of toxin specific activity. We have clarified that the sublytic dose was for live cell imaging experiments, lines 640-641.

*Figure 2A and B have quite different LC50 for starting conditions ({plus minus} 200 HU/ml in A, 600-700 HU/ml in B). Why is it so different? Y-axis has a linear scale in A and a logarithmic scale in B. It would make comparison easier to have the same scale in both panels. *

We agree there is variability between assays. We note that toxin doses change vary in other manuscripts that report toxin mass. For example, aerolysin varies by 10-fold (2 – 20 ng/mL) between figures in Gonzalez et al 2011. We interpret this variation as a common challenge for toxin studies. We mitigate this challenge by including controls for each assay so the relative change can be assessed. We provide additional transparency by including Fig S10 to show batch-to-batch variability of both our toxin preps and assays.

We have changed the scale to linear in Fig 2.*

The letters detonating statistically significant groups are sometimes unclear. For example in Figure 1A and B, PFO belongs to group a and b simultaneously. What does this mean? *

Samples that share letters are not statistically distinct from each other. In the example cited, PFO is not statistically significant compared to all other bars with an a and is not statistically significant compared to all other bars with a b. While confusing at first, the alternative is a mess of stars and bars.

This has been explained in lines 981-985.*

In Figure 8, aerolysin hat a LC50 in cells overexpressing GFP-Dysferin of approximately 1700 HU/ml in A and of approximately 400 HU/ml in B. Why is it so different? *

This is due to intra-assay variation. We include controls for each assay to ensure the trend remains consistent.*

In Figure S1, it is unclear what the plots « all events » vs « single cells » mean. *

We have clarified these plots.*

In the discussion, the authors write « First, survival did not correlate with overexpression, which would be expected if dysferlin acted as Ca2+ sink ». What is meant? GFP-dysferlin overexpression does correlate with survival in Figure 1A. *

We meant that the extent of Dysferlin expression did not correlate with survival. If Dysferlin acted as a calcium sink, cells expressing 100x dysferlin levels should be more resistant than cells expressing 1x dysferlin levels. If Dysferlin needs to serve a cellular function, the brightest cells may not be more resistant (or even be less resistant due to aggregates, etc). We checked to see if the brightest Dysf+ cells had better survival than the dimmest Dysf+ cells. They did not. However, all Dysf+ cells had better survival than Dysf- cells.

We have updated the manuscript (lines 496-498) to reflect these changes.

Significance

*General assessment: The study strength lies in the several possible protection mechanisms that are tested. The weaknesses lie in the contradictions of the results reported here with established mechanisms, *

We disagree with the reviewer that findings that contradict previously proposed mechanisms are a weakness for significance. Instead, we argue this is a strength of our study’s significance. Replication of prior studies’ conclusions using distinct experimental conditions is critical for the reproducibility and rigor of the underlying science, and may give new insights into toxin biology. While we acknowledge the differences in approach, these differences narrow the prior mechanisms that may have been assumed to be widely applicable. The finding that they cannot be replicated in our system suggests one or more of the differences between the studies may drive a critical aspect of aerolysin biology. For example, the Ca2+ difference with Larpin et al could be due to a cellular Ca2+ channel present in HeLa cells that is absent in THP.1/U937 cells.

This distinction is expected to spur additional research in the aerolysin field.

* Advance: The study contradicts previously established results but the experimental conditions used here are quite different to those used in the earlier studies, which makes the comparison quite difficult. As such it does not really fill a gap. *

We have rephrased the significance to better convey both the gap our study fills in membrane repair and the advance that it has made. See lines 99-102, 128, 519-525.*

Audience: The study will be of interest of specialized audience. *

Given the emerging broad importance of membrane repair in response to endogenous pore-forming toxins, and the large gaps in the field of membrane repair, we respectfully disagree with the reviewer. We have revised our significance statements to better convey this broad appeal. See lines 99-102, 128, 519-525.

Reviewer 2

Major

*3. I find the optimisation of lysin concentrations and data presentation quite confusing. I eventually understood, what was done, but I feel that the authors should be able to transform the data and plots so these are more accessible to a reader, eg a simple dose/time-response curves would be very helpful in that respect. For example, in Figure S1E, why does aerolysin appear to be less cytotoxic after 24 hrs than after 1 hr. In principle, I would expect to observe an additive effect, i.e. cell death at 1, 3, 6, 12, and 24 hrs should add to 100%; however, if 100% cells die at 500HU/ml, how can more cells die after 24hrs? Or am I missing something in the experimental design/data presentation? *

We agree that presenting the results from cytotoxicity can be challenging. We use LC50 in the main text because it is easiest to understand. However, we provide all dose-response curves underlying those numbers in the supplemental data. We recently published our approach to assays and data analysis (Haram et al PMID: 36373947) to make it easier to understand.

In Fig S1E, each time point is a distinct assay. In contrast to the approach suggested by the reviewer, where we read the plate at different timepoints, we used different replicates to generate the time points. As a result, the % will not add to 100. Instead, we observe that the majority of cell death occurs in the first hour. We have clarified our discussion of Fig S1E, lines 154-155.

At 24 h, it is possible that cell growth interfered with the assay. The plate has a finite surface area. If control cells are confluent near the start of the assay, but toxin-treated cells are not due to cell death by aerolysin, the growth rates may not be equal. Since our focus is on proximal membrane repair events, and not on late signaling events, pursuing this further is beyond the scope of the current manuscript.

*I also wonder whether using haemolytic units is appropriate (it may well be, if justified), given that the toxins used here have various membrane-binding properties. Wouldn't it make more sense to compare the cytotoxicity using nucleated cells? *

We agree with the reviewer on the need for standardization, and do compare cytotoxicity using nucleated cells (HeLa). Our first level of standardization is the use of hemolytic units instead of toxin mass. This normalizes toxin activity to the ability to kill human red blood cells, which are widely accepted as having minimal membrane repair mechanisms. This gives us a baseline activity, and allows us to control for toxin impurities/differences between toxin preps/toxins. We prefer cytotoxicity over membrane binding for our baseline because it is a functional assay.

After this first level of standardization, we compare the cytotoxicity in HeLa cells. This is one reason why the majority of our assays are performed in HeLa cells—we know how they behave at different toxin doses in our hands, the cells are easy to use, and we can standardize assays in the lab. We included HeLa cells as a control in Fig 5 to show the standardization requested by the reviewer. We split Fig 1 up differently to better convey the results.*

1. The authors use "sublytic" concentrations of aerolysin (64HU) throughout most of the paper, but according to Figure S1C, 50% cells died at that concentration after 1hr, suggesting that when the cells were investigated over a shorter period of time, they were already dying - it's almost like the cells had life support turned off, but still being investigated as though they survived aerolysin treatment. This needs to be clarified or reassessed. *

We agree with the reviewer that we did not track cell survival beyond 45 min in our live cell imaging assays. We labeled cells as ‘surviving >45 min’ to acknowledge the fact that these cells could have died at 46, 47, 60, or 600 min after the experiment ended. We focused on time points earlier than 45 min because proximal membrane repair mechanisms are expected to have occurred in that time, and had time to complete. We have updated the manuscript on lines 214-215.

We next considered the reviewer’s excellent point that the cells alive at 30-40 min could be executing a cell death program. If this were the case, then based on our FACS data (Fig S1C), we would predict ~50% of total cells would be dead by 1 h. From Fig 3A, ~35% of the cells died in the first 45 min. From the remaining 65%, we would predict another 15% dying from this programmed cell death pathway, which would be 15/65 = ~25% of the surviving cells. We did not notice 1/4 of the surviving cells behaving distinctly. For example, the large error bars in 3H is due to a range of cell behaviors that we could not easily subgroup. For individual cells (shown in Figs 6 and 7), there is similarly no clear demarcation of 1/4 of the cells. While we see a gap with pro-aerolysin, that is ~1/3 of the cells (not the expected 1/4), and it is not repeated with aerolysin. While we can’t rule out a cell death program contributing to the top or bottom 1/4 of our results, removing the top or bottom 25% of data points would not alter our major conclusions from the live cell imaging. If a programmed cell death pathway that occurs in the 30-90 min range is identified for aerolysin, it would be interesting to see how that pathway changes repair kinetics. However, that would require identification of the death pathway.

*

1. What effect does the addition of 150mM KCl have on the plasma membrane, trafficking/repair - wouldn't the plasma membrane be depolarised? There were a number of papers by John Cidlowski in mid 2000s, where his team explored the effect of potassium supplementation on apoptosis - this may be worth exploring. *

We thank the reviewer for suggesting these interesting papers. We have explored these papers, and our understanding of them is as follows. Franco et al 2008 PMID: 18940791 shows that ferroptosis is independent of high extracellular K+. This contrasts with Fas-dependent apoptosis, which is suppressed by high extracellular K+. This is consistent with the Cidlowski group’s other work (eg Ajiro et al 2008 PMID: 18294629) and Cohen’s group (eg Cain et al 2001 PMID: 11553634) showing that apoptotic DNA degradation performs better at low K+, and extracellular K+ interferes with apoptosis. Similarly, other papers have shown that NLRP3-activated pyroptosis can be blocked by addition of extracellular K+. Depletion of intracellular K+ inhibits endocytosis and other vesicle trafficking pathways.

While these are good papers, they do not directly relate to our K+ findings, which is that blocking K+ efflux via elevated extracellular K+ levels has no impact on aerolysin-mediated killing. Therefore, to stay focused on the repair pathways, we opted not to include these papers to avoid distracting the reader from our key points. *

1. Figure 3 and accompanied text: it would be more informative to show all the data rather than breaking it down to 45 min. In my view, *

We have added histograms to show when individual cells died during the assay as supplemental Fig S3E. We used the three bins for the exact reason articulated by the reviewer—we wanted to consider cells that died fast vs slow differently. However, in order to interpret the data, a cutoff of 5 min was chosen as optimal. While we agree with the reviewer that the 5 min death could be dismissed, we presented the data to avoid questions about why we omitted those data.*

1. I am curious whether EGTA diffuses into the cytosol through aerolysin pores. If so, then unlike BAPTA-am it would affect Ca inside and outside the cell. *

We agree with the reviewer this is an interesting question. While EGTA might diffuse into the cytosol, its binding properties suggest it would be unsuitable to block cytoplasmic Ca2+ transients (see Nakamura 2019 PMID: 31632263). BAPTA binds to Ca2+ ~40x faster than EGTA, which enables it to capture Ca2+ prior to Ca2+-binding proteins. In contrast, EGTA is thought to be too slow to sequester intracellular Ca2+ before Ca2+-binding proteins. While EGTA might perturb Ca2+ close (

*Are the authors confident that in the absence of extracellular calcium (EGTA treatment), aerolysin formed the pores at all? Have they looked, for example, at intracellular Na/K, or have any other evidence of membrane disruption? *

Prior structural studies suggest that Ca2+ is not required for aerolysin pore formation. For example, Iacovache et al (2011) PMC3136475 induce oligomerization with low salt and pH 2+. Cryo-EM from the same group (Iacovache et al 2016 PMID: 27405240), showed pore formation under similar conditions.

In Fig S3, aerolysin kills in the presence of EGTA at higher concentrations, suggesting that it can form pores when EGTA is present. Also, in Fig 2D, we used Tyrode’s buffer, which was made without Ca2+ or EGTA. We added the indicated amounts of Ca2+ in, and observed a reduction in lysis at low [Ca2+]. This argues against EGTA interfering with toxin oligomerization/pore formation because EGTA was not present, and the toxin still failed to kill.

We have updated the manuscript (lines 203-205) to emphasize this point.*

1. Figure 6 (and some other): I find the designation of statistical significance (a-f) quite confusing, as it is unclear which comparisons are statistically different. Looking at Figure S5, there was no difference between the effect of Annexin depletion on the toxicity of the three lysins. *

Samples sharing the same letter are NOT statistically significant. This is done to avoid a mess of stars and bars with multiple comparisons. This has now been explained in lines 981-985.

For Fig 6/ Fig S5 (now S6), there was a statistically significant difference in LC50 between control siRNA and Annexin knockdowns for SLO. We agree that visually the dose-response curve in Fig S6B looks similar. However, we note that the x-axis is a log2 scale, and the control line is distinct over the 250-1000 region. When we calculate the LC50, these differences give different LC50 values. Over multiple reps, these differences were consistent enough to be statistically different.

Significance

*The paper attempts to address an interesting question of aerolysin pore repair, and it is interesting from the perspective of a potential difference between various pore-forming proteins. *

We agree with the reviewer and thank the reviewer for this assessment.*

The study will be potentially interesting to a broad audience of biochemists/cell biologists and microbiologists working in the field of pore-forming proteins/virulence factors. *

We agree with the reviewer and thank the reviewer for this assessment.

Reviewer 3

*Major comments In the first instance, the authors use a method of assaying the specific lytic activity of aerolysin in comparison to a number of different CDCs. Whilst it is acknowledged that these methods have been published in peer-review papers previously (e.g. Ray et al., Toxins, 2018), it would be great to have more information of how the specific activity is derived. Currently there is a convoluted method that makes a number of assumptions such as, but not limited to, 1) the number of dead cells measured in the FACS experiments is proportional to the activity of the different classes of PFPs however the authors do not show how they account for PFPs leading to loss of cells into debris which would involve a total cell count and *

We thank the reviewer for raising these concerns. We tested these assumptions in our previous papers. We compared the FACS assays to other assays that measure total cells (i.e. MTT assay), and found that the FACS assay corresponds with the MTT findings. These findings were published in Keyel et al 2011 PMID: 21693578 and Ray et al 2018.

Loss of countable events to debris is detected in our assay as saturation of cell death at a number under 100%. Since we perform dose-response curves, we can determine when the killing saturates. This is why loss of countable events does not change our ability to accurately calculate LC50.

2) how the inflection or linear point is identified on individual experiments (e.g. Supp. Fig. 1B, 2A, 2B, 3A, 3B to name a few) and how reliable these points are (e.g showing the data points with model sigmoidal (?) curve and corresponding R values).

This had been calculated manually in the prior version of the manuscript. To address the reviewer’s concern and to improve data quality, we reanalyzed all of our data by fitting our dose-response curves to logistic models, and determining the LC50 using that model. An in-depth explanation of our approach was just published in Haram et al PMID: 36373947, which we now cite (line 821). *

Furthermore, the batch-to-batch variability of protein samples presented in table 1 may be an issue where inactive but folded protein can affect the formation of homo-oligomer pores so more effort to reduce the effects of batch variation would be integral to the foundation of this paper. Given that aerolysin has a very different action on cells then this new characterisation should be provided regardless of what has been previously published by the authors on the activity of CDCs on the cells.*

We agree with the reviewer that batch-to-batch variability is a key concern for pore-forming toxins. To address the concern of batch-to-batch variability and toxin purity, we have added Supplemental Fig S10. In Fig S10C, D, we plot the LC50 against specific activity of each toxin prep when used against control cells. We found a statistical difference in LC50 between two of our toxin preps, but not between any of the others. Notably, there was no association between increasing specific activity and LC50.

Furthermore, we tested the impact of impurities on our toxin prep. While we purify most toxins only using His-beads (obtaining ~40% purity) (Fig S10B), we purified two toxin preps to higher purity (>90%) (Fig S10A). We did not observe differences in LC50 between these toxin preps. The specific activity for these toxins did not increase. We interpret that finding to indicate the gain in specific activity for purity was offset by the loss of specific activity due to prolonged toxin purification.*

• Can the authors provide the raw data for the total FACS observations (scatterplot for all events) and show that there is no significant loss of cells? Or at least there is accountability of the cells? *

Our stop conditions were to collect at least 10,000 gated events instead of running for a set period of time/set volume to determine cell density. We provide example scatterplots in Fig S1A.

* - Can the authors provide more information about how the linear regression on Supp. Fig. 1B and other experiments showing the model sigmoidal curve performed such that this work is more reproducible? *

We agree with the reviewer that using logistic modeling would strengthen the work. To address this concern, we reanalyzed all of our data and switched to logistic modeling. This improved reproducibility for many figures. Changes that add or remove statistical significance to results include Fig 4A, loss of significance between Ca2+/DMSO and BAPTA/DMSO, Fig 6C, loss of significance for siRNA knockdown of A6 vs scrambled for ILY, and Fig 8A/B, gain of statistical significance for GFP-Dysf protecting SLO. We have updated our results accordingly.*

The SEMs of some data points (specific lysis LC50 scatterplots, for e.g. Fig. 2C, 4A, 4C, 8A and fMAX plots, for e.g. Fig. 3B) may not be apparently representative of the skew (e.g. and individual values (including outliers). A clarification of the statistical analysis behind the results may benefit in a clearer understanding of how the SEMs were calculated and presented in the main figures. Also, further elaboration on the meaning of the lettering in the scatterplots (denoted as a, b, c etc.) across the main figures may help improve the interpretation of the data. *

The SEMs were calculated by Graphpad and graphs also generated by Graphpad. To address the reviewer concern, we have switched all places where we plotted individual data points to median with no error bars. This will enable the reader to judge skew, outliers, etc without reliance on error bars.

We have now further elaborated on the lettering in the scatterplots. Samples sharing the same letter are NOT statistically significant. This is done to avoid a mess of stars and bars with multiple comparisons. This has now been explained in lines 981-985.*

Secondly, the authors present interesting results on the significance of Ca2+ on aerolysin's mechanism behind lytic activity and introduces dysfurlin-mediated patch repair as the primary cellular resistance mechanism against aerolysin mediated lysis. Results from Figure 2-4, indicate that extracellular Ca2+ plays a role in aerolysin's function and cell lysis (aerolysin triggers influx of extracellular Ca2+). However, the results presented in figure 8 suggest an impairment of dysferlin translocation from the cytosol to the plasma membrane upon removal of extracellular Ca2+. If this were the case, wouldn't dysferlin impairment sensitise cells to aerolysin? Thus, in these sets of experiments it seems that Ca2+ is a confounding factor.*

We agree that Ca2+ is a confounding factor, which is one reason we aimed to define better membrane repair mechanisms in response to different pore-forming toxins. Our interpretation is that Ca2+ triggers a death pathway that overcomes repair, and that aerolysin toxicity is due to the activation of this pathway. In this case, the impairment of Ca2+-dependent pathways does not reduce survival because the extent of damage is reduced/not present. Figuring out this death pathway is beyond the scope of the present manuscript, but a one future direction in which we are interested. This would also account for differences observed in different cell lines.*

• Can the authors further elaborate on how the function of dysferlin in protecting cells against aerolysin contrasts to how aerolysin kills cells? *

We have added the requested discussion to our manuscript, lines 519-525.

*Finally, it is also interesting to see that cells deploy different resistance mechanisms between different families of pores. In saying that, the usage of CDCs seems to be inconsistent between each set of results. For example, intermedilysin (ILY) was used in the siRNA knockdown experiments but not in others such as Ca2+ influx assays, while PFO was only used for the initial set of results. A comment on this would benefit in understanding the rationale for selecting certain CDCs for each set of experiments. *

We thank the reviewer for raising this point. We used SLO as the primary CDC in all the experiments because it is the CDC we have best characterized and have extensively published on. We included PFO in initial experiments to give readers a better idea of how multiple CDCs compare to aerolysin in target cells. However, since we’ve previously published on PFO, including it for later experiments would have increased cost and time of experiments without providing new knowledge.

We used ILY because it binds to the GPI-anchored protein human CD59, so its binding determinant is more similar to aerolysin, which binds GPI-anchored proteins. We included it where practical to determine the extent to which targeting may change repair responses. Since ILY does not bind to murine cells, it was omitted from experiments using murine cells.

We have added the rationale to the manuscript on lines 138-140.*

Minor comments Results (Nucleated cells are more sensitive to aerolysin and CDCs) - A statement of the EC50 values of aerolysin and CDCs from the haemolytic assays would be beneficial to compare activities between the two pores. *

The hemolytic activity is defined as the EC50 for the toxin in human red blood cells. The specific activity enables comparison of toxin activity, which is reported in Table 1. We have now added Supplementary Fig S10 which further plots the aerolysin and SLO specific activities against LC50 so that the reader can better assess batch-to-batch variability. In this study, we did not use enough batches of the other toxins to make this analysis useful for them.

* - Figure 1A: As stated in the introduction, pro-aerolysin exists as a precursor that is functionally inactive unless activated by trypsin, furin or potentially other proteases. It would benefit the reader if an explicit statement were made about this activity and how it may come about in HeLa and 3T3 cells. Why is pro-aerolysin not shown in the Casp 1/11-/- BMDM cells? *

The cell surface furin activity that activates aerolysin is not well-characterized across different cell types. We have revised the manuscript (line 76) to indicate these activities are present on the cell membrane.

We omitted pro-aerolysin from the Casp1/11-/- BMDM because we performed those experiments earlier in the study before we started including pro-aerolysin. Based on the other results, we judged that the time and resource costs of adding pro-aerolysin in this system outweighed the gain to the story.

* - Figure 1C: It was stated that "Casp 1/11 -/- Mo were ~100 fold more sensitive to pro-aerolysin and aerolysin compared to PFO and SLO" but did not show the activity for pro-aerolysin in these cells. *

We thank the reviewer for catching this typo, and have corrected this statement (line 172).

* - Supp fig 1E: Shouldn't 24 hr incubation of aerolysin to HeLa cells result in 100% specific lysis? *

We agree with the reviewer that these results were surprising. At 24 h, it is possible that cell growth interfered with the assay. The assay well has a finite surface area. If control cells are confluent near the start of the assay, but toxin-treated cells are not due to cell death by aerolysin, the growth rates between control and experimental wells may not be equal. Since our focus is the proximal membrane repair events, and not the late signaling events, pursuing this further is beyond the scope of the current manuscript.

* (Delayed calcium flux kills aerolysin-challenged cells) - What is the intracellular concentration of K+ normally in cells? Similarly, what is the intracellular concentration of Ca2+? *

Intracellular K+ is ~140 mM (see Ajiro et al 2008 PMID: 18294629), while cytosolic Ca2+ is ~100 nM at rest.

* - Figure 2C: Based on the description in the methods and results, both buffers are supplemented with 2 mM Ca2+ but one buffer (RPMI) shows more killing with SLO and ILY. Does this mean that both buffers contain 2 mM CaCl2? If so, what are the other potential reasons why one buffer enabled greater potency in CDCs? *

RPMI has 0.4 mM Ca2+ prior to Ca2+ supplementation. However, the 2.4 mM Ca2+ did not provide improved protection compared to RPMI alone (See Fig 2 in Ray et al 2018).

We suspect the various amino acids added to RPMI promote membrane integrity and account for the difference from Tyrode’s buffer. Glycine has previously been implicated in promoting membrane repair, but at higher concentrations than it is present in RPMI (0.133 mM in RPMI vs the mM concentrations used to protect cells). If other amino acids also protect, and/or why they protect is beyond the scope of the present work.

* - Figure 3H: The data for aerolysin (WT) would greatly benefit for comparison to the inactive mutant (and indicate the sustained Ca2+ increase). *

We have added this comparison, and updated the figure legend, line 1015.

* - Supplementary Video V1: The addition of Triton X-100 permeabilises cells; however, this wasn't evident in (A). - Video V2: Similar to previous comment on Supplementary Video V1 (for B). *

In V1A, the video was cut short to fit the play time with other videos. From addition, the triton takes a few minutes to diffuse to the cells and permeabilize them. In V2B, the cells do become permeabilized as shown by loss of the Ca dye. The cells are out of focus, which is why the nucleus TO-PRO is not detected.*

(Calcium influx does not activate MEK-dependent repair) - Figure 4A: Effective ionic concentration inside and outside cell is increased (if intracellular Ca2+ becomes chelated); therefore, Ca2+ may enter the cell by passive diffusion or transport by other intrinsic Ca2+ channels. *

There is already a very steep concentration gradient for Ca2+. The cytosolic Ca2+ is ~0.1 uM, compared with growth medium at 400 uM or assay buffer at 2400 uM. Chelation of the intracellular Ca2+ is not expected to increase Ca2+ import from outside the cell.*

(Caveolar endocytosis does not protect cells from aerolysin) - Figure 5C: What is the purpose of using HeLa cells as a control? *

We included HeLa cells to demonstrate the toxin was active and to rule out batch-to-batch variability as one interpretation of the reduced killing of differentiated 3T3-L1 cells.

* - "..with Alexa Fluor 647 conjugated pro-aerolysin K244C" - this should be introduced earlier as it was initially mentioned in Supp. Figure 3C. *

We have now introduced this earlier at line 190, instead of 300

* - Murine fibroblasts were used earlier (Figure 1). Following from this result (where the WT can be used as a positive control), can MEFs be used instead of adipocytes to see whether caveolar endocytosis plays any role in cellular resistance? *

The 3T3-L1 cells are murine fibroblasts prior to differentiation. Since they can also be differentiated into adipocytes, we used them instead of MEFs. The other reasons we used them include the availability of Cavin knockout cells, and the extensive caveolae present in adipocytes. We included analysis of 3T3-L1 prior to differentiation them in Fig 5B.

* - Further comment on the increased resistance of K5 knockout would benefit on the mechanism of aerolysin-mediated cytolysis. *

We agree further characterization of this line would be interesting in the future. At the present, however, any further comment would be speculative on our part. Since the resistance was not replicated in the second CRISPR line, we suspect it is either an unexpected mutation(s) in the cell line that arose during routine cell culture, or off-target effect(s) from the CRISPR used to generate the line.

* (Annexins minimally resist aerolysin) - Supplementary video V3 - it seems that annexin A6 is recruited to the membrane, to a greater extent (and also quicker) than SLO. This suggests that annexin recruitment is a cellular response against aerolysin challenge. *

We agree with the reviewer that annexins are recruited to the membrane during repair. However, individual knockdown did not enhance death. This is one reason we believe functional studies (i.e. cytotoxicity) are necessary when studying the cell biology of repair events. Recruitment of the protein, and it promoting repair may be two different things.

In V3, three of the SLO-challenged cells have translocated by the time focus is restored. In contrast, the first aerolysin cells translocate ~10 min. One complicating factor is that A6 cycles back off the membrane with the SLO challenge.

* o SLO also shows A6 recruitment (arrows pointed). However, supplementary figure 6B does not clearly illustrate this. *

Given the 45 min time scale, the rapid initial membrane enrichment is hard to see on the graph.

* - As annexin A1 is sensitive to calcium, further comment on the significance of intracellular/extracellular calcium in annexin A1 recruitment and aerolysin challenge would explain observations in Figure 4A. *

We have updated the manuscript, line 242 to include annexins and dysferlin as Ca2+-binding proteins in our discussion of intracellular calcium.*

(Patch repair protects cells from aerolysin) - Supplementary video V4 - the intensity decreases for the inactive mutant; is this due to lysis? *

We included TO-PRO in the experiment to rule out lysis. Since the cells remain in focus, we interpret the lack of TO-PRO to indicate no cellular lysis.

*- The next paragraph sounds like a contradiction: "GFP-dysferlin localized to the plasma membrane and vesicles independently of extracellular Ca2+ (Fig 8C D, Video V5) o Followed by "To study the Ca2+ dependency of dysferlin, we removed extracellular Ca2+ with 2 mM EGTA and challenged with sublytic toxin doses...found less depletion of dysferlin from cytosol". *

We thank the reviewer for pointing out our unclear language. In the second section, we intended to refer to dysferlin positive vesicles. We have rephrased the manuscript (lines 388-395) to clarify that we are focused on Ca2+-dependence of vesicle fusion, not steady-state.*

(Methods) - Table 1: The values presented in the methods section are, overall, confusing and require clarification. *

We have added Fig S10, and discussion of toxin activity and purity in the methods (lines 634-641) to provide further clarity on toxin activity.

* o 10-fold difference in SLO and PFO WT - do the authors think this might change the interpretation between different figures? *

We do not. The reason is that we changed the membrane affinity between SLO and PFO (Ray 2018), and this switches the properties of the respective toxins without changing their yields.

* o Understood how the haemolytic activity was calculated (referred to work in 2012), but how was the haemolytic unit originally derived? *

It was derived as a measure of activity for toxins by determining the EC50 in RBCs for a given toxin. Since species type of RBC and other factors can change the reported activity, we have normalized to using human red blood cells. This lets us assay human-specific toxins like ILY along with other toxins.

* o How were these values (from table 1) derived to toxin concentrations used for killing nucleated cells? *

Full discussion of our assay was recently published in Haram et al 2022 PMID: 36373947. For the cytotoxicity assays, we use the hemolytic activity. Suppose from Table 1, the toxin stock is 1.5 x10^5 HU/mL. Then to prepare a 2x working toxin stock, we dilute the toxin to 4 x10^3 HU/mL (this is a 1 in 37.5 dilution). To get the range of concentrations used in the dose response curve, we perform a 2-fold serial dilution. Finally we mix equal volumes of toxin and cells, giving us the final 1x toxin activity (2 x10^3 HU/mL for the highest concentration in this example).

* o Therefore, an EC50 haemolytic curve showing the activities for all toxins would greatly facilitate in understanding the derivation of values for table 1.*

The hemolytic unit already incorporates the EC50 hemolytic curve. 1 HU is the EC50 of the toxin in the human RBCs.

* - Flow cytometry assay: What is meant by gating out the debris? And would debris also contribute to the count in dead cells? *

We illustrate our gating strategy in Fig S1. The debris falls in the front left corner of the plot, and includes electronic noise, non-cellular debris and cellular fragments. Since one cell could give rise to multiple pieces of debris, we exclude the debris from analysis.

* o What was added as the high PI control? *

In Fig S1A, the high dose of toxin was used for maximal killing. In our cell populations, there is a low level (2-5%) of dead cells that serve as a control for PI staining. In the past, we’ve used 0.01% triton to validate permeabilization of the cells. We have also compared PI uptake with MTT assays (Keyel et al 2011, Ray et al 2018) to confirm that the PIhigh cells are dead.

*Elaborating reviewer #2's comment 7 regarding the addition of EDTA : with respect to measuring the binding if fluorescently labelled aerolysin, how can the authors differentiate between full functional pores versus prepores/incomplete pores? *

This requires electron microscopy, which is the beyond the scope of our current study. However, prior work and Fig 2D show that aerolysin forms pores without the need for Ca2+ (see next point).

How else can the authors validate whether aerolysin remains functional in the presence of EDTA?

Prior structural studies suggest that Ca2+ is not required for aerolysin pore formation. For example, Iacovache et al (2011) PMC3136475 induce oligomerization with low salt and pH 2+. Cryo-EM from the same group (Iacovache et al 2016 PMID: 27405240), showed pore formation under similar conditions.

In Fig S3, aerolysin kills in the presence of EGTA at higher concentrations, suggesting that it can form pores when EGTA is present. Also, in Fig 2D, we used Tyrode’s buffer, which was made without Ca2+ or EGTA. We added the indicated amounts of Ca2+ in, and observed a reduction in lysis at low [Ca2+]. This argues against EGTA interfering with toxin oligomerization/pore formation because EGTA was not present, and the toxin still failed to kill.

We have updated the manuscript (lines 203-205) to emphasize this point.

Significance

*While the work has investigated in-depth cellular resistance mechanisms, the significance and benefits of this study are unclear. For example, the authors have used different human cell lines to dissect how these cells are affected by different pores but have not stated the significance and potential benefit of studying these cell lines. Further elaboration in this aspect may increase the relevance of the study, to an audience who is interested in the field of infection and disease. *

We have updated our significance to better convey our advance, which is explained on lines 99-102, 128, 519-525. We also added benefits of testing the cell lines chosen on lines 167-168, and 277-278. We plan to add muscle cells to address the dysferlin points, which has relevance to necrotizing soft-tissue infections.

Description of analyses that authors prefer not to carry out

Not applicable

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Referee #3

Evidence, reproducibility and clarity

Summary

This body of work by Thapa & Keyel explores the differences in cellular resistance mechanisms between two different pore families (aerolysin versus CDCs). Herein, the authors were able to elucidate the toxin activities across a variety of different nucleated cells, using the haemolytic assay as a reference for normalising activity. Their findings revealed that, in general, aerolysins were relatively more potent than CDCs at damaging certain nucleated cell lines. Furthermore, the authors performed an exploration of different resistance mechanisms, including MEK-dependent repair, annexins, and patch repair by dysfurlin. The work provides some supporting evidence that patch repair is the main mechanism that cells deploy to prevent aerolysin-mediated cytotoxicity. Overall, the amount of work that was put in to craft the manuscript was impressive and the manuscript showed potential prospects in further investigating 1) mode of aerolysin killing in nucleated cells and 2) the role of patch repair and function of dysferlin in cellular resistance against aerolysin.

Major comments

In the first instance, the authors use a method of assaying the specific lytic activity of aerolysin in comparison to a number of different CDCs. Whilst it is acknowledged that these methods have been published in peer-review papers previously (e.g. Ray et al., Toxins, 2018), it would be great to have more information of how the specific activity is derived. Currently there is a convoluted method that makes a number of assumptions such as, but not limited to, 1) the number of dead cells measured in the FACS experiments is proportional to the activity of the different classes of PFPs however the authors do not show how they account for PFPs leading to loss of cells into debris which would involve a total cell count and 2) how the inflection or linear point is identified on individual experiments (e.g. Supp. Fig. 1B, 2A, 2B, 3A, 3B to name a few) and how reliable these points are (e.g showing the data points with model sigmoidal (?) curve and corresponding R values).

Furthermore, the batch-to-batch variability of protein samples presented in table 1 may be an issue where inactive but folded protein can affect the formation of homo-oligomer pores so more effort to reduce the effects of batch variation would be integral to the foundation of this paper. Given that aerolysin has a very different action on cells then this new characterisation should be provided regardless of what has been previously published by the authors on the activity of CDCs on the cells.

• Can the authors provide the raw data for the total FACS observations (scatterplot for all events) and show that there is no significant loss of cells? Or at least there is accountability of the cells?
• Can the authors provide more information about how the linear regression on Supp. Fig. 1B and other experiments showing the model sigmoidal curve performed such that this work is more reproducible?

The SEMs of some data points (specific lysis LC50 scatterplots, for e.g. Fig. 2C, 4A, 4C, 8A and fMAX plots, for e.g. Fig. 3B) may not be apparently representative of the skew (e.g. and individual values (including outliers). A clarification of the statistical analysis behind the results may benefit in a clearer understanding of how the SEMs were calculated and presented in the main figures. Also, further elaboration on the meaning of the lettering in the scatterplots (denoted as a, b, c etc.) across the main figures may help improve the interpretation of the data.

Secondly, the authors present interesting results on the significance of Ca2+ on aerolysin's mechanism behind lytic activity and introduces dysfurlin-mediated patch repair as the primary cellular resistance mechanism against aerolysin mediated lysis. Results from Figure 2-4, indicate that extracellular Ca2+ plays a role in aerolysin's function and cell lysis (aerolysin triggers influx of extracellular Ca2+). However, the results presented in figure 8 suggest an impairment of dysferlin translocation from the cytosol to the plasma membrane upon removal of extracellular Ca2+. If this were the case, wouldn't dysferlin impairment sensitise cells to aerolysin? Thus, in these sets of experiments it seems that Ca2+ is a confounding factor.

• Can the authors further elaborate on how the function of dysferlin in protecting cells against aerolysin contrasts to how aerolysin kills cells?

Finally, it is also interesting to see that cells deploy different resistance mechanisms between different families of pores. In saying that, the usage of CDCs seems to be inconsistent between each set of results. For example, intermedilysin (ILY) was used in the siRNA knockdown experiments but not in others such as Ca2+ influx assays, while PFO was only used for the initial set of results. A comment on this would benefit in understanding the rationale for selecting certain CDCs for each set of experiments.

Minor comments

Results

(Nucleated cells are more sensitive to aerolysin and CDCs)

• A statement of the EC50 values of aerolysin and CDCs from the haemolytic assays would be beneficial to compare activities between the two pores.
• Figure 1A: As stated in the introduction, pro-aerolysin exists as a precursor that is functionally inactive unless activated by trypsin, furin or potentially other proteases. It would benefit the reader if an explicit statement were made about this activity and how it may come about in HeLa and 3T3 cells. Why is pro-aerolysin not shown in the Casp 1/11-/- BMDM cells?
• Figure 1C: It was stated that "Casp 1/11 -/- Mo were ~100 fold more sensitive to pro-aerolysin and aerolysin compared to PFO and SLO" but did not show the activity for pro-aerolysin in these cells.
• Supp fig 1E: Shouldn't 24 hr incubation of aerolysin to HeLa cells result in 100% specific lysis?

(Delayed calcium flux kills aerolysin-challenged cells)

• What is the intracellular concentration of K+ normally in cells? Similarly, what is the intracellular concentration of Ca2+?
• Figure 2C: Based on the description in the methods and results, both buffers are supplemented with 2 mM Ca2+ but one buffer (RPMI) shows more killing with SLO and ILY. Does this mean that both buffers contain 2 mM CaCl2? If so, what are the other potential reasons why one buffer enabled greater potency in CDCs?
• Figure 3H: The data for aerolysin (WT) would greatly benefit for comparison to the inactive mutant (and indicate the sustained Ca2+ increase).
• Supplementary Video V1: The addition of Triton X-100 permeabilises cells; however, this wasn't evident in (A).
• Video V2: Similar to previous comment on Supplementary Video V1 (for B).

(Calcium influx does not activate MEK-dependent repair)

• Figure 4A: Effective ionic concentration inside and outside cell is increased (if intracellular Ca2+ becomes chelated); therefore, Ca2+ may enter the cell by passive diffusion or transport by other intrinsic Ca2+ channels.

(Caveolar endocytosis does not protect cells from aerolysin) - Figure 5C: What is the purpose of using HeLa cells as a control? - "..with Alexa Fluor 647 conjugated pro-aerolysin K244C" - this should be introduced earlier as it was initially mentioned in Supp. Figure 3C. - Murine fibroblasts were used earlier (Figure 1). Following from this result (where the WT can be used as a positive control), can MEFs be used instead of adipocytes to see whether caveolar endocytosis plays any role in cellular resistance? - Further comment on the increased resistance of K5 knockout would benefit on the mechanism of aerolysin-mediated cytolysis.

(Annexins minimally resist aerolysin)

• Supplementary video V3 - it seems that annexin A6 is recruited to the membrane, to a greater extent (and also quicker) than SLO. This suggests that annexin recruitment is a cellular response against aerolysin challenge. o SLO also shows A6 recruitment (arrows pointed). However, supplementary figure 6B does not clearly illustrate this.
• As annexin A1 is sensitive to calcium, further comment on the significance of intracellular/extracellular calcium in annexin A1 recruitment and aerolysin challenge would explain observations in Figure 4A.

(Patch repair protects cells from aerolysin)

• Supplementary video V4 - the intensity decreases for the inactive mutant; is this due to lysis?
• The next paragraph sounds like a contradiction: "GFP-dysferlin localized to the plasma membrane and vesicles independently of extracellular Ca2+ (Fig 8C D, Video V5) o Followed by "To study the Ca2+ dependency of dysferlin, we removed extracellular Ca2+ with 2 mM EGTA and challenged with sublytic toxin doses...found less depletion of dysferlin from cytosol".

(Methods)

• Table 1: The values presented in the methods section are, overall, confusing and require clarification.
  • 10-fold difference in SLO and PFO WT - do the authors think this might change the interpretation between different figures?
  • Understood how the haemolytic activity was calculated (referred to work in 2012), but how was the haemolytic unit originally derived?
  • How were these values (from table 1) derived to toxin concentrations used for killing nucleated cells?
  • Therefore, an EC50 haemolytic curve showing the activities for all toxins would greatly facilitate in understanding the derivation of values for table 1.
• Flow cytometry assay: What is meant by gating out the debris? And would debris also contribute to the count in dead cells?
  • What was added as the high PI control?

Referees cross-commenting

Elaborating reviewer #2's comment 7 regarding the addition of EDTA : with respect to measuring the binding if fluorescently labelled aerolysin, how can the authors differentiate between full functional pores versus prepores/incomplete pores? How else can the authors validate whether aerolysin remains functional in the presence of EDTA?

Significance

The work presents a foundation to further investigate into the mechanism of aerolysin function, following the discovery of the role of extracellular Ca2+ in its activity. As aforementioned, the role of dysferlin in resisting aerolysin also has potential, but the limitations of this work were discussed including the absence of performing a dysferlin knockout, although performing this experiment may help to strengthen the current finding.

While the work has investigated in-depth cellular resistance mechanisms, the significance and benefits of this study are unclear. For example, the authors have used different human cell lines to dissect how these cells are affected by different pores but have not stated the significance and potential benefit of studying these cell lines. Further elaboration in this aspect may increase the relevance of the study, to an audience who is interested in the field of infection and disease.

Section for special notes to the editor:

My major area of expertise and contribution to this paper is in the analysis and interpretation of activity (lytic) assays.

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Referee #2

Evidence, reproducibility and clarity

The current study explored an interesting question of aerolysin pore repair mechanism. An unusual feature of aerolysin is that unlike many other pore-forming proteins its pores remain "open" over a longer period of time, and this affects ion homeostasis influencing cell death and inflammatory response. Eventually, aerolysin pores are repaired, but what governs this process remains unknown.

In my opinion, the paper has several unresolved issues, some of which the authors mentioned in their discussion.

1. The effect of dysferlin overexpression does not indicate that patch repair is a protective mechanism or that dysferlin plays a significant role in aerolysin resistance. The authors should knock out dysferlin and assess cell resistance to lysis.
2. ESCRT complex was shown to play a role in plasma membrane repair following mechanical damage or perforin treatment of cells (Jimenez 2014, and Ritter, 2022). Whether ESCRT is important in aerolysin pore repair can be assessed by knocking out the Chmp4b gene or overexpressing dominant-negative mutant of VPS4a, E228Q.
3. I find the optimisation of lysin concentrations and data presentation quite confusing. I eventually understood, what was done, but I feel that the authors should be able to transform the data and plots so these are more accessible to a reader, eg a simple dose/time-response curves would be very helpful in that respect. For example, in Figure S1E, why does aerolysin appear to be less cytotoxic after 24 hrs than after 1 hr. In principle, I would expect to observe an additive effect, i.e. cell death at 1, 3, 6, 12, and 24 hrs should add to 100%; however, if 100% cells die at 500HU/ml, how can more cells die after 24hrs? Or am I missing something in the experimental design/data presentation? I also wonder whether using haemolytic units is appropriate (it may well be, if justified), given that the toxins used here have various membrane-binding properties. Wouldn't it make more sense to compare the cytotoxicity using nucleated cells?
4. The authors use "sublytic" concentrations of aerolysin (64HU) throughout most of the paper, but according to Figure S1C, 50% cells died at that concentration after 1hr, suggesting that when the cells were investigated over a shorter period of time, they were already dying - it's almost like the cells had life support turned off, but still being investigated as though they survived aerolysin treatment. This needs to be clarified or reassessed.
5. What effect does the addition of 150mM KCl have on the plasma membrane, trafficking/repair - wouldn't the plasma membrane be depolarised? There were a number of papers by John Cidlowski in mid 2000s, where his team explored the effect of potassium supplementation on apoptosis - this may be worth exploring.
6. Figure 3 and accompanied text: it would be more informative to show all the data rather than breaking it down to <5, 5-45 and >45 min. In my view, <5 min is an acute death due to lysis, where the toxins overcame all the protective mechanisms (membrane repair). If anything, I would dismiss that acute cell death altogether, and focused on the cells that survived the initial onslaught.
7. I am curious whether EGTA diffuses into the cytosol through aerolysin pores. If so, then unlike BAPTA-am it would affect Ca inside and outside the cell. Are the authors confident that in the absence of extracellular calcium (EGTA treatment), aerolysin formed the pores at all? Have they looked, for example, at intracellular Na/K, or have any other evidence of membrane disruption?
8. Figure 6 (and some other): I find the designation of statistical significance (a-f) quite confusing, as it is unclear which comparisons are statistically different. Looking at Figure S5, there was no difference between the effect of Annexin depletion on the toxicity of the three lysins.

Referees cross-commenting

I agree with the critique raised by the other two reviewers.

I am also happy to revise the time required to complete revisions to 3-6 months, but feel that even this may be optimistic considering substantial technical problems raised by Reviewer 1.

Significance

The paper attempts to address an interesting question of aerolysin pore repair, and it is interesting from the perspective of a potential difference between various pore-forming proteins.

The study will be potentially interesting to a broad audience of biochemists/cell biologists and microbiologists working in the field of pore-forming proteins/virulence factors.

My expertise is the biochemistry and cell biology of pore-forming proteins.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Thapa et al studied cellular mechanisms of membrane repair following pore forming toxin insult, namely aerolysin and CDCs. Out of four mechanisms tested, they show that under their conditions patch repair is the only mechanism able to counter aerolysin injury. The study is interesting but raises some concerns.

Major:

The authors conclusions contradict established results, which they cite. Yet experimental conditions are not similar in two ways: toxin concentration-wise and toxin treatment duration-wise. While we appreciate the efforts of the authors to standardize the concentration of toxins used based on hemolytic units, we note that the concentrations used are very much higher than in the other studies cited. Indeed, based on table 1, materials and methods, and the various experiments, aerolysin has a LC50 of approximately 200 HU/ml, which corresponds to about 2 ug/ml. This is approximately 200x more concentrated than for example in Gonzalez et al 2011 and Larpin et al. 2021. It makes the validity of direct comparison with those studies questionable. We noticed that the authors activate pro-aerolysin at high concentration (in the range of 1 to 5 mg/ml) and at room temperature. In our experience, under these concentration, activation leads to immediate oligomerization and massive precipitation. The final concentration of active toxin is thus unknown. The authors keep their cells in toxin-containing medium for the whole duration of the experiments, typically 45 minutes. This is in stark contrast with 45 seconds to 3 minutes transient exposure to toxin in Huffman et al 2004.

The authors do not report binding and oligomerization assays of the toxins. The only figure showing a western blot (fig. 7) is of low quality and shows unexpected observations. Aerolysin Y221G mutant is expected to bind and oligomerize. Yet, no band is present at about 250 kDa (expected oligomer) or at about 47 kDa (monomer). In addition, in aerolysin lanes (1 and 2) the oligomer is saturated, seems to be covering three lanes, indicating a possible spill-over.

Finally, while the patch repair hypothesis is interesting, it is unclear why the authors decided to overexpress dysferlin in cell lines that normally do not express it. Sure, there is a repair phenotype but this phenotype is artificially introduced. Dysferlin is not expressed at all in HeLa cells. Furthermore, dysferlin is not expressed in epithelial cells, which are the prime target of aerolysin. Why then focus on this protein? In order to show that patch repair is indeed protecting cells against aerolysin, the authors should disrupt patch repair of the cells under study and observe and increased toxicity.

Minor:

The graphic legends should be boxed out to be clearly separated from the data. In Figure 4A, it is mixed up with the data.

Some western blots are saturated, e.g. B-actin in figure 4B. Full blots should be provided.

In the methods, aerolysin sublytic dose for HeLa cells is specified at 62 HU/ml. In figure 5C and D, 31 HU/ml kills more than 50% of HeLa cells. This is not compatible.

Figure 2A and B have quite different LC50 for starting conditions ({plus minus} 200 HU/ml in A, 600-700 HU/ml in B). Why is it so different? Y-axis has a linear scale in A and a logarithmic scale in B. It would make comparison easier to have the same scale in both panels.

The letters detonating statistically significant groups are sometimes unclear. For example in Figure 1A and B, PFO belongs to group a and b simultaneously. What does this mean?

In Figure 8, aerolysin hat a LC50 in cells overexpressing GFP-Dysferin of approximately 1700 HU/ml in A and of approximately 400 HU/ml in B. Why is it so different?

In Figure S1, it is unclear what the plots « all events » vs « single cells » mean.

In the discussion, the authors write « First, survival did not correlate with overexpression, which would be expected if dysferlin acted as Ca2+ sink ». What is meant? GFP-dysferlin overexpression does correlate with survival in Figure 1A.

Referees cross-commenting

I notice quite a number of overlapping points between my comments and those of the other reviewers. In particular concerning the varying definition of sublytic concentrations and the need of a dysferlin-KO.

Significance

General assessment: The study strength lies in the several possible protection mechanisms that are tested. The weaknesses lie in the contradictions of the results reported here with established mechanisms, and in the statement that a cellular process that has been artificially introduced in the experimental system is the cellular protection mechanism against aerolysin attack. In order to prove that this process is a bona fide protection mechanism, the authors should show that it is present without the need of overexpressing a protein that is not expressed at all either in the used cell line (HeLa), or in the natural cellular target of aerolysin (epithelial cells). The significance of the proposed protection mechanism is therefore questionable.

Advance: The study contradicts previously established results but the experimental conditions used here are quite different to those used in the earlier studies, which makes the comparison quite difficult. As such it does not really fill a gap.

Audience: The study will be of interest of specialized audience.

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Reply to the reviewers

Manuscript number: RC-2022-01668

1. General Statements

We are grateful to reviewers for their thorough, insightful, and highly constructive feedback.

GENERAL REPLY #1.

We clarify a major misunderstanding. All instances of the phrase “failure of phagocytosis” or__ “phagocytic dysfunction” should be re-worded as “persistence of dead tissue”__ or simply “necro-slough.” The word “phagocytic” contains an implication of “cells” or micro-scale issues, which was not our thinking. We apologize for the ambiguity. Our claim is strictly about the millimeter-scale tissue outcome, not about cell activities to cause the tissue outcome. Please consider how strongly this miscommunication may have affected reviewers’ requests.

The relevant hypothesis statement now reads as follows: “Given that pressure ulcers often have slough or eschar, we hypothesize that mPI will have persistence of dead tissue in the wound bed, and that sterile mPI will have slough, despite the absence of bacterial biofilm.” This is a clinically-oriented claim about the relationship between bacterial infection and sloughing, not a cell biology claim about the relationship between macrophages and efferocytosis. We do not believe (and we do not wish to hypothesize) that mPI phagocytes are present and healthy while refusing to perform efferocytosis. To the contrary, such cells appear to be dead or absent at day 3 of mPI. Cells cannot clear debris when they are dead/absent. To satisfy the requests of peer review, we will perform some measurements looking for altered efferocytosis activity in monocytic cells, but we caution that the results might be negative.

GENERAL REPLY #2.

Reviewers asked us to characterize specific details of the immune system, especially for monocytes/macrophages. We did already measure many general immune-related factors at different timepoints, and found that surprisingly few of the general immunology analytes had any statistical significance (Supplementary Tables 3, 5 and 6), despite the large fold-changes seen in damage-related epitopes of oxidative stress.

We wish to avoid making any claims about the immune system in mPI, other than the absence of intact immune cells in untreated day-3 mPI wounds, and the DFO-induced increase in the presence/influx of immune cells at days 7 & 10. These serendipitous findings about immune cells are not required for any of the five chief hypotheses listed in our introduction. To characterize which cell types “should have been” present, and why they are absent, cannot possibly be established by the Reviewer’s request for greater rigor in the CTX-versus-mPI comparison, because CTX is the wrong comparison for that purpose.

To address reviewers’ requests, we provide multiple additional experiments characterizing limited aspects of the immune system. We are interested in how mPI wounds diverge from the dominant theory of what causes non-healing wounds. The dominant theory is that non-healing wounds are caused by excessive inflammation due to pre-existing morbidities (e.g., diabetes) and/or pro-inflammatory disruption (e.g., infection) that extend the duration of the inflammation phase. According to this theory, prolonged inflammation is what causes damage and blocks the granulation phase from progressing. Our mPI model violates expectations in two ways. Firstly, the dominant theory expects a non-healing wound to have elevated presence/infiltration of immune cells, but we found absence of intact immune cells at the earliest timepoint. The second is that mPI levels of oxidative damage were inversely correlated with immune cell abundance, suggesting that immune cells were not the largest source of oxidative damage. As expected, oxidative damage was highly correlated with poor healing (and was downstream of myoglobin iron). In summary, we will perform multiple additional studies toward “better describing the immune response ensuing the injury” which will promote the shared goal of understanding mPI and elucidating what the DFO drug is accomplishing.

We have one minor question about editorial policy for re-displaying the same control images for multiple experiments.

Reviewer Two initial comments (minor)

“- Figure 5 C, E, G: please provide illustrations for control treatment.

- Figure 6 K, L, M: please provide illustrations for control treatment."

The controls for Figure 5C, 5E, and 5G were already shown in Figure 2 (2I, 2L and 2B), and we hesitate to show them again without permission from the editor to duplicate figures. Similarly, controls for Figure 6K, 6L and 6M are already shown in Figure 2F-G.

2. Description of the planned revisions

__PLANNED ADDITION #1. __Measuring the iron system via immuno-staining.

*Reviewer Two initial comments: *

“2. Is myoglobin also released in the injured tissue after CTX and how does it compare to mPI (Mb+ surface area, quantity)?

• What about expression levels of proteins involved in heme/iron detoxifying proteins haptoglobin and hemopexin? Are they present in the injured tissue and are they differentially expressed between types of injury and mouse genotypes? Same goes for their receptors (CD163 and CD91, respectively): are they differentially expressed on macrophages found in the injured tissue?*

- Is hemoglobin found mPI and CTX wounds from WT or Mb-/- mice?”

Reviewer Two cross-comments:

“The way I understand the authors' work, instead of broadening the scope of the work with a cellular mechanism (phagocytic dysfunction), I would rather suggest the authors to focus on strengthening the description of their model of injury (mPI) versus CTX, on key points that are known to influence tissue repair/regeneration as well as their main findings: evaluation of the injury's surface area, __myoglobin deposition/accumulation in the wound, __better describing the immune response ensuing the injury. Hence my major comments 1 to 7.”

Authors' reply: We interpret this feedback to mean that measurements of myoglobin and iron detoxification factors would be help explain why mPI has higher iron and what consequences the iron may have. However, we believe the collapse or destruction of vessels in mPI (described below in the section for Completed Revision 2) might suffice to explain why iron-containing waste accumulates in mPI while the same waste gets removed in CTX. Furthermore, iron detoxification factors might be unable to enter the wound without the blood vessels.

For Planned Addition #1, we will perform the following five measurements, which should provide data for two core issues: globin protein presence in the wound, and iron detoxification factors in the wound. The methods we will perform are immunostaining for the following factors, comparing mPI against CTX at day 3 (each treated with saline and no other drugs, each with n=3 replicates).

1. Myoglobin
2. Hemoglobin
3. Hemopexin
4. Haptoglobin

5. Haptoglobin receptor CD163 Expected outcomes, regarding myoglobin abundance at day 3 post-injury in mPI vs CTX:

6. If Myoglobin is elevated in mPI vs CTX, then this finding would corroborate the increased ferric iron in mPI (measured by Prussian blue staining). It would also support the interpretation that myoglobin is the source of the excess iron that decreases upon myoglobin knockout.

7. If Myoglobin is not elevated in mPI vs CTX, then our myoglobin hypothesis could be in question and/or the myoglobin might have degraded to a state that remains redox active without binding the anti-myoglobin antibody (as occurs for hemoglobin [6]) and/or the day 3 timepoint could be too early/too late to observe the phenomenon. Expected outcomes, regarding iron detoxification factors (hemopexin, haptoglobin and CD163) at day 3 post-injury in mPI vs CTX:

8. If hemopexin and haptoglobin and/or haptoglobin receptor CD163 are elevated in mPI vs CTX, some readers will interpret this to mean that mPI has increased heme and/or increased scavenging of extracellular myoglobin/hemoglobin. Elevated hemopexin would corroborate our finding that Prussian blue staining is increased in mPI. One serious problem for interpretation of haptoglobin is that the haptoglobin-myoglobin complex has low affinity, while the haptoglobin-hemoglobin complex has high affinity, and some hemoglobin is probably present. Therefore, we also perform hemoglobin staining. Note also that CD163 is often used as a biomarker for “M2” macrophages, in addition to being the receptor for haptoglobin.

9. If hemopexin, haptoglobin, and/or haptoglobin receptor CD163 are not elevated in mPI vs CTX, some readers might interpret the measures to be irrelevant because the loss of blood vessels in mPI might prevent involvement of circulating factors. Other readers might interpret it to mean that mPI did not need, or did not utilize increased levels of the circulating factors. Other considerations are that the globin/heme source could degrade and the day 3 timepoint might be too early or too late to observe the phenomena of interest.
10. We cannot guarantee the primary antibodies will pass quality control and provide desired results. PLANNED ADDITION #2. Describing the immune response in vivo and in vitro.

Reviewer One initial comments:

“It would be interesting to see if myoglobin prevents monocyte or macrophage migration/chemotaxis. Another aspect is how cells reach the injured area… Given that the study is already quite huge with numerous experiments, the reviewer is reluctant to ask for additional experiments…

Also the points mentioned above, about the role of myoglobin in immune cell infiltration and the role of myoglobin in the vessel properties should be at least discussed, if they are not experimentally addressed.”

*Reviewer Two initial comments: *

“8. The in vitro experiments with macrophages could be further supported by in vivo experiments, where types of injury (mPI vs. CTX) and mouse genotypes (Mb-/- vs. WT) could be evaluated for the ability of macrophages to perform efferocytosis: coupling apoptotic cell detection (Tunel staining) to macrophage immunostaining. Quantification of overlapping signal would give some information (albeit indirect) regarding the macrophages' ability to clear the tissue from dead cells. From my perspective, this would be the minimal set of data required to highlight a potential "efferocytic failure" in mPI.”

Reviewer Two cross-comments:

“The way I understand the authors' work, instead of broadening the scope of the work with a cellular mechanism (phagocytic dysfunction), I would rather suggest the authors to focus on strengthening the description of their model of injury (mPI) versus CTX, on key points that are known to influence tissue repair/regeneration as well as their main findings: evaluation of the injury's surface area, myoglobin deposition/accumulation in the wound, better describing the immune response ensuing the injury. Hence my major comments 1 to 7.

Beyond these points, the authors can then re-assess whether or not to include the role of myoglobin on monocyte/macrophage infiltration on the site of injury and the phagocytic activity of these recruited macrophages as part of this manuscript.”

Reviewer One cross-comments:

“Point 8 should be investigated if the authors wish to claim about efferocytosis.”

Authors' reply: We interpret this to mean that most readers will want to see more cell-specific and macrophage-specific data to complement the tissue experiments and molecular experiments. The specific choice of experiments is left up to us, but reviewers both agree something more is needed.

For Planned Addition #2, we will perform the following five measurements, which should provide quality data for at least three core issues: macrophages ex vivo, neutrophils ex vivo, and in vitro response of macrophages to myoglobin treatment. The methods we will perform are the following:

1. Perform Tunel staining alongside macrophage (F4/80) immuno-staining, to look for whether macrophages have engulfed apoptotic debris. We will compare mPI+Saline versus mPI+DFO at day 7, to see whether iron depletion affects the amount of engulfed debris inside macrophages.
2. Perform quadruple staining of pan-macrophage marker F4/80, pro-inflammatory macrophage marker iNOS, pro-regenerative macrophage marker Arginase-1, and DAPI nuclear stain.
3. Perform immuno-staining for Ly6G, a marker of neutrophils, and myeloperoxidase, a marker of neutrophil extracellular traps (NETs/NETosis).
4. Perform immuno-staining for CD38 and CD86. CD38 is a marker of CD4+, CD8+, B and Natural Killer cells. CD86 is a marker of dendritic cells, macrophages, B cells and other antigen-presenting cells. For greater information content, this staining might be multiplexed with the neutrophil staining, if antibody optimization is successful.
5. Measure the impact of Myoglobin on monocytic cell functions in vitro. We will test naïve and M1-differentiated RAW264.7 monocytes/macrophages, with or without treatment with myoglobin. The highest priority is to measure efferocytosis activity, but we will consider three functional assays: phagocytosis, efferocytosis, and transwell migration.

For the ex vivo studies (items 1-4 above), we will compare mPI+Saline versus mPI+DFO at day 7, using CTX+saline at day 3 as the positive control (n=3 per group). The in vitro treatment groups are naïve and M1-differentiated RAW264.7 monocytes/macrophages treated with or without myoglobin. The positive control is H2O2 treated RAW264.7 cells. The experiments will be carried out in quadruplicates.

Expected results for co-localization of Tunel+ F4/80 in mPI vs CTX.

• If Tunel+viable F4/80 co-localization is decreased in mPI vs CTX, then some readers might interpret a decrease in phagocytic activity by macrophages, which might help explain the persistence of dead tissue in mPI.
• If Tunel+viable F4/80 co-localization is not decreased in mPI vs CTX, then some readers may interpret that iron and its scavenger DFO cause no difference in the phagocytic function of macrophages, but some might question the timepoint or methods.

• Note that if we cannot see Tunel+F4/80 co-localization in day 3 samples of CTX injury (the positive control condition), then we consider that the assay has failed. Expected results for immuno-staining of Ly6G, myeloperoxidase, CD38 and CD86 in mPI vs CTX.

• If Ly6G, CD38, and CD86 are observed inside cells, they can indicate categories of immune cells present in the wounds. If observed extracellularly, they will be interpreted as debris from cells previously present.

• Myeloperoxidase is expected to be extracellular in the case of extracellular traps.

• Any observations will reflect only the timepoint measured, which may be before or after the peaok for that analyte. Note that we cannot guarantee that these antibodies will pass quality control and provide useful results, and we only have enough tissue samples to measure each analyte in triplicate. Expected results for cell-based assays of RAW264.7 cells when treated with myoglobin.

• If myoglobin-loaded macrophages exhibit decreased cell functions of efferocytosis, phagocytosis, and/or migration in vitro, then some readers might see this as the cellular mechanism for persistence of dead tissue and sloughing. However, such a finding would not rule out other causes of necro-slough. For example, the relative primacy of macrophages and fibroblasts in efferocytosis is subject to debate.

• If no change is detected, many readers will interpret this to mean mPI macrophages have no change in cell function after myoglobin loading.
• Our claims are unaffected either way, because what we see are dead immune cells and delayed presence/influx into the wound, and cells cannot clear debris when they are dead/absent.

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

Completed Revision #1. Major text amendments

Reviewer One initial comments:

“Given that the study is already quite huge with numerous experiments, the reviewer is reluctant to ask for additional experiments. Rather, the reviewer suggests to reshape the text, remove unnecessary details to get straight to the points and to emphasize the important result. …Discussion sections about oxidative stress, endogenous iron, prevention studies, antiDAMPs strategies, slough and debridement are poorly informative and poorly referenced and should be either removed or shortened.”

Reviewer Two cross-comments:

“I also agree with Rev#1's assessment that some claims should be toned down… __Beyond these points, the authors can then re-assess whether or not to include __the role of myoglobin on monocyte/macrophage infiltration on the site of injury and the phagocytic activity of these recruited macrophages as part of this manuscript.”

Authors' reply: We have amended the main text as follows:

• Changed the title to omit the term “phagocytic dysfunction”.
• Changed the text to emphasize tissue physiology and not evoke concepts of cell biology. Changed terminology so that all “failure of phagocytosis” will be written as “persistence of dead tissue.”
• Shortened our discussion and conclusion by 33%, especially the sections entitled “the context of oxidative stress”, “anti-DAMP strategies”, and “debridement of slough.” Our abstract now says, “Unlike acute injuries (from cardiotoxin), mPI regenerated poorly with a lack of viable immune cells, persistence of dead tissue (necro-slough), and abnormal deposition of iron.” The old version had said, “mPI regenerated poorly with a lack of viable immune cells, failure of phagocytosis….”

Completed Revision #2. Surface area and vascular comparisons between CTX and mPI injuries.

*Reviewer Two initial comments: *

“I find the direct comparison made between the two types of injury, CTX and mPI, difficult to interpret. From my perspective, a more rigorous and systematic comparison between the two models of injury would be key to convincingly convey the findings of this work, especially regarding key features impacting repair.

1. • Time for tissue repair not only depends on the type of injury, but also on the extent of the injury. In other words__, how the mPI and CTX models compare in terms of surface of injured tissue__ (and resulting ischemia)?” Reviewer Two cross-comments:*

“The way I understand the authors' work, instead of broadening the scope of the work with a cellular mechanism (phagocytic dysfunction), I would rather suggest the authors to focus on strengthening the description of their model of injury (mPI) versus CTX, on key points that are known to influence tissue repair/regeneration as well as their main findings: evaluation of the injury's surface area,….”

Authors' reply: We interpret the feedback to mean that the surface area of injured muscle should be comparable between CTX and mPI in order to claim that the tissue repair is different between the two injuries. We will provide the requested measurements showing similarity between the wounds, but we disagree with the premise that one should seek similarity. To that end, we will provide additional data (not requested), showing other forms of dissimilarity. Our scientific claims don’t rely on comparisons between CTX and mPI, and we urge readers to refrain from direct comparisons between dissimilar wounds.

We have revised the transferred manuscript as follows:

1. Added requested data (Suppl. Table 1) showing that both CTX and mPI have comparable size of dead muscle at the initial timepoint. To avoid making claims about CTX, we will delete the word “normal,” we will delete our phrase saying CTX lacks the dysfunctions seen in mPI, and we will explain that the purpose of CTX is to show a dissimilar example of muscle regeneration after an acute injury.
2. Added supplementary images (Suppl. Fig 2) showing dramatic differences in vasculature between CTX injury and mPI. Add accompanying text will explain that the goal of examining different types of wounds is model-description and hypothesis-generation, not hypothesis-testing Completed Revision #3: “Minor” edits suggested

Minor Edit #1

Suppl. Fig 4 is added to show intact immune cells at the wound margin and the absence of intact immune cells in the compressed region 3 days after mPI. This is as per Reviewer One’s suggestion to change Suppl. Fig 6 and call it in the results section that, “In the discussion section, there is reference to a SupplFig6, which seems to be not the good one in the document. In the FigS6 described in the text, it is mentioned that cells are kind of "stopped" at the boundaries of the damage… mPI Discussion end of page 10. Unfortunately, suplFig6 is missing (and is not called in the result section).”

Minor Edit #2

Main Fig 2L and Main Fig 5E have been changed to more representative images of HO-1 fluorescence in Day 3 saline- and DFO-treated mPI respectively, as per Reviewer Two’s minor comment, “Figure 2: HO-1 staining seem decreased in mPI compared to CTX and thus doesn't support the quantifications. Please 2x-check quantifications and images to provide consistent quantifications-illustrations pairing.”

Minor Edit #3

Suppl. Fig 5 (previously Suppl. Fig 3) has concentration and treatment times added to the figure caption as per Reviewer Two’s minor comment, “Provide concentrations and treatment times in figure legends (sup Fig3).”

Minor Edit #4

Suppl. Fig 6 (previously Suppl. Fig 4) has DNA gel electrophoresis results (Suppl. Fig 6D) added as requested by Reviewer Two in minor comment, “Show all the data mentioned in the manuscript (DNA gel electrophoresis supp fig 4)”

Minor Edit #5

Suppl. Fig 8, Suppl. Fig 10 and Suppl. Fig 12 have labels added to the image sets as per Reviewer Two’s minor comment, *“Missing information in supp Fig 5 A-D: which images from WT or Myb-KO?” *

Minor Edit #6

Suppl. Fig 11A-D have a different, more representative image set to show F4/80, CitH3 and DAPI triple-stain in saline-treated mPI (day 3). DAPI staining was not shown previously (only F4/80 and CitH3.)

Minor Edit #7

Suppl. Fig 12E has a blue dashed line added to the graph for the level of MerTK fluorescence in uninjured skinfold.

Minor Edit #8

Clarifying text and citation on the BODIPY 581/591 fluorescent probe that we used has been added in the Results section, as per Reviewer Two’s minor suggestion, “Bodipy is not a probe for lipid peroxidation. Due to its lipophilic nature, this dye can be used as a generic lipid satin to image intracellular lipid depots. Therefor the experiments using bodipy as a proxy for lipid peroxidation is incorrect and derived conclusions erroneous. Modulation in bodipy signals probably reflects modulation of intracellular lipid deposition.”

Minor Edit #9

The section, “Data availability”, which discloses the link to the Zenodo database containing the mice numbers and primary data has been moved from Suppl. Methods (Suppl. Text) to Methods in the main text.

Minor Edit #10

The acknowledgements section has been updated.

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

Reviewer Two initial comments:

“4. Does in situ Mb supplementation in Mb-/- mice worsens mPI repair to an extent that is comparable to WT mice?”

Authors' reply: Further study of knockout mice (Mb-/-) was mentioned by Reviewer Two, but the reviewer did not prioritize this experiment. We will not carry this out because we have already spent many years breeding descendants of our Mb-/- mice, trying to generate more Mb-/- pups, but the later years of breeding have had zero live births of homozygous knockouts. Because we have reached the ethical limit of wasted animals, any further study of myoglobin knockout would require an entirely new conditional knockout system, which is a long-term future investment.

Citations:

[1] Wang Y, Lu J, Liu Y. Skeletal Muscle Regeneration in Cardiotoxin-Induced Muscle Injury Models. Int J Mol Sci. 2022 Nov 2;23(21):13380.

[2] Averin AS, Utkin YN. Cardiovascular Effects of Snake Toxins: Cardiotoxicity and Cardioprotection. Acta Naturae. 2021 Jul-Sep;13(3):4-14.

[3] Naldaiz-Gastesi N, Goicoechea M, Alonso-Martín S, Aiastui A, López-Mayorga M, et al. Identification and Characterization of the Dermal Panniculus Carnosus Muscle Stem Cells. Stem Cell Reports. 2016 Sep 13;7(3):411-424.

[4] Ahmed AK, Goodwin CR, Sarabia-Estrada R, Lay F, Ansari AM, et al. (2016). A non-invasive method to produce pressure ulcers of varying severity in a spinal cord-injured rat model. Spinal Cord, 54(12), 1096–1104.

[5] Turner CT, Pawluk M, Bolsoni J, Zeglinski MR, Shen Y, et al. (2022). Sulfaphenazole reduces thermal and pressure injury severity through rapid restoration of tissue perfusion. Scientific Reports, 12(1), 12622.

[6] Bahl N, Du R, Winarsih I, Ho B, Tucker-Kellogg L, Tidor B, et al. (2011) Delineation of lipopolysaccharide (LPS)-binding sites on hemoglobin: from in silico predictions to biophysical characterization. J Biol Chem. 286(43), 37793-803.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this manuscript, Jannah and colleagues highlight a pathophysiological mechanism involving myoglobin for the poor repair capacity of ulcerative pressure wounds. The authors modeled muscle pressure injury (mPI) using a magnet and compared it to cardiotoxin (CTX)-induced muscle injury. They show a significant delay in repair kinetics for mPI compared to CTX, recapitulating the notoriously poor repair process associated with ulcerative pressure injuries. Using mice genetically invalidated for myoglobin (Mb), they show an improved mPI recovery, with improved tissue repair quality over a shorter period of time. Mechanistically, the authors link the poor repair of mPI to the oxidative and pro-inflammatory effect of Mb released from injured skeletal muscle fibers.

Major comments:

The authors hypothesis regarding the role of Mb in the pathophysiology of ulcerative pressure injuries is interesting. However, the work here seems quite preliminary with major points remaining to be clarified before considering reaching the author's conclusion. I find the direct comparison made between the two types of injury, CTX and mPI, difficult to interpret. From my perspective, a more rigorous and systematic comparison between the two models of injury would be key to convincingly convey the findings of this work, especially regarding key features impacting repair. My major comments are listed below.

1. Time for tissue repair not only depends on the type of injury, but also on the extent of the injury. In other words, how the mPI and CTX models compare in terms of surface of injured tissue (and resulting ischemia)?
2. Is myoglobin also released in the injured tissue after CTX and how does it compare to mPI (Mb+ surface area, quantity)?
3. Does Mb co-injection with CTX mimics mPI injury in terms of inflammation and repair kinetics?
4. Does in situ Mb supplementation in Mb-/- mice worsens mPI repair to an extent that is comparable to WT mice?
5. A better characterization of the inflammatory between types of injury and mice (Mb-/- vs. WT) before and after 3- and 10-days post-injury would be very informative. Comparing the relative proportions of leukocyte populations would provide valuable information regarding the kinetics of the repair process.
6. Macrophages in particular play a central role in the orchestration of tissue repair, through their immunomodulation abilities. On the same token, characterizing macrophage infiltrates (number per surface area of injured tissue) and phenotype would potentially provide valuable information to link observed differences between types of injuries to Mb. Ideally, assessment of leukocyte and macrophages infiltration and populations would be analyzed by flow cytometry after injured (vs. uninjured) tissue dissociation (enzymatic or mechanical). Otherwise, although less quantitative, this can also be done by cell infiltration using specific immunostaining and quantification (cell number/injured tissue surface area).
7. Macrophage phenotype (inflammatory vs. anti-inflammatory/reparative) can be achieved by RTqPCR, using well-define combination of mRNA encoding proteins associated with inflammatory (e.g. iNos, Cox-2, Cd86) or anti-inflammatory (Ym1, Arg-1, RELMa, Cd206).
8. The in vitro experiments with macrophages could be further supported by in vivo experiments, where types of injury (mPI vs. CTX) and mouse genotypes (Mb-/- vs. WT) could be evaluated for the ability of macrophages to perform efferocytosis: coupling apoptotic cell detection (Tunel staining) to macrophage immunostaining. Quantification of overlapping signal would give some information (albeit indirect) regarding the macrophages' ability to clear the tissue from dead cells. From my perspective, this would be the minimal set of data required to highlight a potential "efferocytic failure" in mPI.
9. What about expression levels of proteins involved in heme/iron detoxifying proteins haptoglobin and hemopexin? Are they present in the injured tissue and are they differentially expressed between types of injury and mouse genotypes? Same goes for their receptors (CD163 and CD91, respectively): are they differentially expressed on macrophages found in the injured tissue?

Minor comments:

• Figure 2: HO-1 staining seem decreased in mPI compared to CTX and thus doesn't support the quantifications. Please 2x-check quantifications and images to provide consistent quantifications-illustrations pairing.
• Figure 5 C, E, G: please provide illustrations for control treatment.
• Figure 5J: it would have been nice to add Mb-/- mice to the comparison.
• Figure 6 K, L, M: please provide illustrations for control treatment.
• Figure 8: please maintain consistency in the way you convey data between timepoints: area of regenerated (E, F) or unregenerated (G) tissue.
• Bodipy is not a probe for lipid peroxidation. Due to its lipophilic nature, this dye can be used as a generic lipid satin to image intracellular lipid depots. Therefor the experiments using bodipy as a proxy for lipid peroxidation is incorrect and derived conclusions erroneous. Modulation in bodipy signals probably reflects modulation of intracellular lipid deposition.
• Provide concentrations and treatment times in figure legends (sup Fig3).
• Show all the data mentioned in the manuscript (DNA gel electrophoresis supp fig 4)
• Indicate the number of experimental repeats and the statistical tests used in the figure legends.
• Missing information in supp Fig 5 A-D: which images from WT or Myb-KO?
• Is hemoglobin found mPI and CTX wounds from WT or Mb-/- mice?

Referees cross-commenting

I have read the report from Reviewer#1 and below are my cross-comments.

I agree with Rev#1's minor comments. I also agree with Rev#1's assessment that some claims should be toned down as data don't support them. The phagocytic dysfunction is certainly one of them, for the reasons mentioned, but not the only one. Indeed, I believe that virtually all the claims could use some dampening to various extent because the level of evidence is not very high throughout. A more rigorous description of the injury model would address this point in my opinion (narrower scope with a demonstration).

The way I understand the authors' work, instead of broadening the scope of the work with a cellular mechanism (phagocytic dysfunction), I would rather suggest the authors to focus on strengthening the description of their model of injury (mPI) versus CTX, on key points that are known to influence tissue repair/regeneration as well as their main findings: evaluation of the injury's surface area, myoglobin deposition/accumulation in the wound, better describing the immune response ensuing the injury. Hence my major comments 1 to 7.

Beyond these points, the authors can then re-assess whether or not to include the role of myoglobin on monocyte/macrophage infiltration on the site of injury and the phagocytic activity of these recruited macrophages as part of this manuscript.

Significance

The field of tissue repair and regeneration is an exciting field and improving our understanding of the molecular mechanisms involved in muscle tissue injury has clear and impactful clinical applications.

The pathophysiological mechanism involving Mb that the author address in this work has the potential to interest both basic science and clinical researchers and can potentially benefit not only the field of skeletal muscle regeneration but also the field of cardiac remodeling.

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Referee #1

Evidence, reproducibility and clarity

Summary: The study by Nasir et al. investigates the healing properties of skeletal muscle after a pressure injury and the impact of myoglobin in this process. First, they compared cardiotoxin versus pressure injuries and showed that the latter heals slowly and badly (this is shown through a large series of parameters). They then used myoglobin deficient mice or WT mice treated with the iron chelator DFO to show that in the absence of myoglobin, there is an improvement of the regeneration process.

Major comments:

The study is well written, clear, and the experiments are carefully presented and conducted. Although the text is usually very detailed and nicely referenced, some of the claims should be dampened. Notably the title since the phagocytic dysfunction is not evidenced by the results, not the wound enlargement (since DFO has no impact on it). <br /> Also the text is very long, notably the discussion, which contains 18 sections (!) and several sections are not very informative and poorly referenced, looking more as a thesis dissertation than as an article discussion.

Concerning immune cells, the conclusion cannot be that myoglobin impedes their phagocytic function. All the data concur that in the absence of myoglobin there are more immune cells in the regenerating muscle at day 3. Consequently, more macrophages will lead to a better cleansing of debris. Thus, the difference would not rely on phagocytic properties per se, but more on the number of macrophages that arrive at the site of injury. It would be interesting to see if myoglobin prevents monocyte or macrophage migration/chemotaxis. Another aspect is how cells reach the injured area. In the discussion section, there is reference to a SupplFig6, which seems to be not the good one in the document. In the FigS6 described in the text, it is mentioned that cells are kind of "stopped" at the boundaries of the damage. This is very interesting. If the vessels are physically flattened or squashed by the injury, extravasation can not occur properly, in comparison with cardiotoxin. Then the role of myoglobin in extravasation, or in the "reshaping" of the vessels after the removal of the magnet would be interesting to investigate. Of note, in the myoglobin deficient mice, the vascular network is increased, favoring immune cell infiltration.

Given that the study is already quite huge with numerous experiments, the reviewer is reluctant to ask for additional experiments. Rather, the reviewer suggests to reshape the text, remove unnecessary details to get straight to the points and to emphasize the important results. Also the points mentioned above, about the role of myoglobin in immune cell infiltration and the role of myoglobin in the vessel properties should be at least discussed, if they are not experimentally addressed.

Minor comments:

• Page 5: "The panniculus layer of mPI was nearly devoid of intact immune cells." It is not clear here if the authors refer to the absence of immune cells or to damage of immune cells present in the injured area.
• Page 6: "In summary, measures of innate immune response became less abnormal after Mb knockout". Cardiotoxin injury is not the "normal" situation since this kind of injury is not physiological and is highly inflammatory as compared with others (Hardy et al., Plos One 2016).
• Discussion sections about oxidative stress, endogenous iron, prevention studies, antiDAMPs strategies, slough and debridement are poorly informative and poorly referenced and should be either removed or shortened.
• Discussion end of page 10. Unfortunately, suplFig6 is missing (and is not called in the result section).

Referees cross-commenting

I agree with the rev#2's review and later comments. His comments are quite complementary to those I raised. If the author have the capacity to make the experiments that are proposed by Rev#2, it would be super nice. Point 8 should be investigated if the authors wish to claim about efferocytosis.

Significance

This study is of interest because it provides insights on muscle regeneration after an injury that may occur in daily life just as contusion, or crush, to the contrary of the whole muscle necrosis induced by cardiotoxin (the main model used in the field). In that aspect, it is more physiological and of interest for the readers in the fields of in muscle regeneration and tissue trauma. The study is descriptive, but is very well conducted and well discussed. Additional experiments investigating the impact of myoglobin on vessel properties/extravasation of immune cells would raise the impact of the study but the study is publishable as it is (with editing as suggest above).

The field of expertise of the reviewer is muscle regeneration and inflammation.

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I thank the Referees for their...

Referee #1

1. The authors should provide more information when...

Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...

Response: We expanded the comparison

Minor comments:

1. The text contains several...

Response: We added...

Referee #2

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Referee #3

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate). In this paper the authors develop an engineered uterus-like microenvironment to recapitulate peri-implantation development of the whole mouse embryo ex vivo. This new model (3E-uterus) is used for mechanistic studies of embryo implantation. They hint that integrin-mediated adhesion of the embryo to the uterine wall is required for peri-implantation mouse development. The authors use this model also to study the role of tension for embryo development. They postulate that release of tension from the polar side of the embryo upon implantation allows for extra embryonic development. By using mathematical modeling of the implanting embryo as a wetting droplet, the authors link the embryo shape dynamics to the underlying changes in trophoblast adhesion and suggests that the adhesion-mediated tension release facilitates egg cylinder formation. Finally, the authors uncover the role of coordination between trophoblast motility and embryo growth, where trophoblast mobility displaces the Reichart's membrane giving the embryo space to grow. In summary, the authors technically advance the field of developmental biology by providing a model to study peri implantation morphogenesis of the mouse embryo.

Major comments:

• Are the key conclusions convincing?

The key conclusions the authors derive from their experiments are somewhat convincing. Suggested experiments below will strengthen their claims. - Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

Claim 1: The 3E-uterus is representative of mouse embryo peri-implantation. To claim this a more extensive validation of the embryos cultured in their 3E uterus both via scRNA seq and IF for pluripotency, visceral and parietal endoderm markers is required. It is also interesting that embryos cultured in the 3E-uterus lose the correct timing of development. Could the authors please comment on this? scRNA seq of the embryos cultured in their system at different timepoint (i.e. Day 1-3) compared to control pre, peri and post implantation embryos could help answer this question.

Claim 2: The release of tension from the polar side upon implantation allows for extra embryonic development. To quantitatively measure the difference in tension before and after implantation is technically very challenging. However, this paper could benefit of further validations including IF stainings for markers such as E-cadherin, F-actin and Phospho myosin. In addition to this, treatments with Y27 and blebbistatin of the embryo would allow to further study the role of cell tension on embryo implantation. Finally, a laser ablation experiment at the cell junctions of the polar region before and after implantation would help to answer this question but this could be technically challenging due to the curvature nature of embryos.

Claim 3: Integrin-mediated adhesion between the trophoblast and the uterine matrix is required for in utero-like transition of the blastocyst to the egg cylinder. In Figure 2a the authors show that embryos cultured in 3E-uterus without RGD do not develop and hypothesize this is due to lack of integrin binding. A control experiment using a non-integrin binding peptide is beneficial here.

Claim 4: The spatial orientation of the embryo plays a key role in mouse peri implantation development. In Figure 5i-j, the authors place embryos in a downward (i) and upward (j) orientation. Could the authors also please comment on whether they believe the orientation, the way the embryo feels the gravity plays a role in implantation? Is the amount of space that the embryo has to grow in the limiting factor on development? Could the authors use 3E-uterus models with different lengths (by using molds with different spacing) to see the role of geometry and space that the embryo has for trophoblast mobility and embryo growth. What would happen if the embryo were very close to the bottom of the hydrogel?

Claim 5: A mathematical model based on the wetting droplet recapitulates the embryo in their system. Could the authors comment on whether their mathematical model considers proliferation, and would proliferation have an impact on the system's kinetics? What is the role of polar TE proliferation and how does that influence the trophectoderm morphology? If the embryo is geometrically confined, can the authors exclude that this confinement is influencing cell shape? - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

In this technical advance paper, the claims will become more robust with the suggested experiments above. Claims of implantation should be changed to accurately reflect that the 3E-uterus models peri implantation as there is no invasion in the 3D hydrogel matrix. In addition to this, the uterine cells are missing which are required to fully recapitulate the mechanisms of embryo peri-implantation. - Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments.

3- 6 months will allow the authors to address all questions above. Yet, the laser ablation experiment might be difficult to perform due to the curvature of the embryo. - Are the data and the methods presented in such a way that they can be reproduced?

We appreciate the details of the materials and methods section particularly of the imaging.<br /> - Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

• Laminin staining in Figure 2A is only done in in vitro embryos but not in in vivo embryos. Could the authors add the missing staining?

• It would be beneficial to have both active and normal integrin stainings in E4.5 embryos.
• Could the authors provide stainings for mesenchymal markers for E4.5 and D2 3E uterus?
• Can the authors comment on Figure Supp. 3D where the timing seems to be flipped?
• Why was 600 um chosen for the depth of the 3E-uterus?
• Are prior studies referenced appropriately?

How do the findings in this paper relate to the findings in Weberling et al (PMID 33472064), where they show that in vivo, the polar trophectoderm exerts physical force upon the epiblast, causing it to transform from an oval into a cup shape? - Are the text and figures clear and accurate?

Overall the text and figures are clear and accurate. In figure 2E and 2G, the outline covers the staining. Would it be possible to have it without the outline in the supplementary? - Do you have suggestions that would help the authors improve the presentation of their data and conclusions? It would be very informative to have for each panel in which a representative image is used for that image to be marked into the quantified data (graphs).

Overall, the manuscript is very well written and the conclusions are informative and clear.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The advance presented in this paper is technical. In this methodology paper, the authors use their novel model to investigate the mechanics of embryo peri-implantation and hint at new conceptual findings such as the role of wetting properties of the embryo onto the ECM of the uterus. - Place the work in the context of the existing literature (provide references, where appropriate).

Since embryos become hidden in the womb upon implantation, ex vivo cultures provide an experimental setting to monitor, measure and manipulate embryonic development. Ex vivo culture of peri-implantation (mouse) embryos so far relied on embryonic growth on 2D plastic surfaces (PMID: 4930085, 4562729 and 24529478) or 3D bioreactors (PMID: 33731940). Although important, these assays do not recapitulate the interaction with the uterine cells and ECM (the in vivo scenario). In this study initial steps are taken to recapitulate the interaction of the embryo with the uterine ECM during peri-implantation. Uterine cells are however missing from this new system, which is important for understanding the full mechanism of implantation. - State what audience might be interested in and influenced by the reported findings.

Developmental biologists - 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.

Bioengineer, bioinformatician and developmental biologists working with embryo models and hydrogels. There is not sufficient expertise to evaluate the mathematical modeling.

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Referee #2

Evidence, reproducibility and clarity

The authors developed a new method of ex vivo culture of mammalian embryos. This engineered uterus recapitulates some features of peri-implantation development of the mouse embryo. The authors show that integrin adhesion to the uterine wall through integrin beta 1 is required for proper peri-implantation. They also demonstrate collective migration of the trophoblast on the synthetic hydrogel surface. The authors interpret their results through the physics of wetting, which allows them to conclude that a release of tension enables shape changes in the embryo. Finally, light sheet imaging allows the authors to visualize the interplay between growth and collective motion.

Major

1. The article will be of potential interest to a broader community than mammalian embryo peri-implantation researchers. This broader community will likely not be familiar with the structure and nomenclature of the embryo and surrounding tissues. The introduction of terms in the second paragraph of the introduction should be paralleled by a comprehensive image in Fig. 1. This image should clarify what is considered apical and basal in this context. Similarly, when the model is introduced a more comprehensive scheme should also be provided.
2. The failure of 2D hydrogels to support mouse blastocysts through peri-implantation (Supp Fig. 1) is insufficiently described. Some panels in this figure and not mentioned in the main text. This discussion should be expanded, especially considering that 2D approaches has been quite successful. A detailed discussion of the authors' cylinder approach compared to the best 2D systems published should be provided (Govindasamy et al, for example).
3. Is the hydrogel purely elastic or viscoelastic? The mechanical properties of the hydrogel (viscoelasticity and degradability) should be presented in the main text.
4. The authors call the finding that integrins are required for peri-implantation "striking", but a role for integrins in this process is are already known (see Sutherland et al, for example). The novelty of the authors findings in this regard should be better presented.
5. Figures 2ef (in utero) and 2gh (3E-uterus) show rather different results. In uterus, pERM and ZO1 look quite compartmentalized in the outer region. This is not the case in 3E-uterus shown in Figure 2gh. These data do not seem to support an agreement between in utero and 3E-uterus as mentioned in the text.
6. The authors claim that mTE cells lose cell polarity upon adhesion to the uterine matrix and acquire mesenchymal properties. This claim should be clarified. Cells protrude and become migratory but invasion seems to be collective, suggestive that epithelial features such as cadherin adhesion remain. Are these cells mesenchymal or are they simply epithelial cells with motile capacity (as in wound healing, for example)? How do mesenchymal vs epithelial features compare between in utero and 3E-uterus?
7. If I understand correctly, the model assumes that tension of the droplet-medium interface and is the same in the upper and lower sides of the embryo. However, the mechanical and geometrical properties of cells in both sides are quite different. Is the assumption of same tension justified? Can these tensions be measured or inferred to test this assumption?
8. Along similar lines, attributing a surface tension to a system that is thick (ie several cell layers) and that undergoes apical constriction (ie a bending modulus) is an oversimplification that should be justified. Cells in the pTE change (potentially) their apical, basal and lateral tension during apical constriction. How do these three components relate to what the model simply refers as tension? Additionally, how does the presence of a bending moment alter the wetting picture?
9. The physics of wetting were recently generalized to include additional terms attributed to active components (main associated with polarity, see works by Alert and Casademunt). These active components are not explicitly taken into account in the authors' model. Are they not needed? A brief discussion of this aspect should be provided.
10. In utero, the cavity in which the embryo is implanted is created during implantation. In this situation, the analogy with wetting seems harder to establish because the embryo spreads as it forms the cavity. How does this alter the authors interpretation?
11. The first paragraph of the supplementary note refers to Fig. 4D. This reference here does not seem correct.

Referees cross-commenting

The three of us coincide in appreciating the novelty and potential impact of the new method.

There is an agreement between all 3 referees to request additional evidence of how well the 3E-uterus captures the in vivo phenomenon. I believe the suggestions provided by my two colleagues in this regard are on point and seem feasible for the applicants within a 6 month period.

I also agree that tension measurements with laser ablation (or other inference techniques) would provide stronger support to the model.

Significance

This article provides an important technical advance to study peri-implantation of the mammalian embryo beyond current methods based on 2D substrates. This work will be of interest to the community of early mammalian embryogenesis but also to the broader field of engineering multicellular systems.

As list above, main limitations concern 1) The extent to which their method properly captures peri-implantation, 2) The novelty of some of the authors observations, 3) The soundness of the theoretical model.

My expertise is in experimental biophysics of multicellular systems.

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Referee #1

Evidence, reproducibility and clarity

Summary:

To recapitulate mouse peri-implantation development ex vivo, the authors engineered a uterus-like microenvironment by fabrication of topographically patterned hydrogels and identified the roles of the physical interaction between embryo and hydrogels for egg cylinder formation. Notably, integrin-mediated adhesion between trophoblast and matrix facilitates egg-cylinder shape. Moreover, Live-imaging with light-sheet microscopy led them to propose the hypothesis that the interaction between embryos and hydrogels appeared to be described by a droplet wetting process.

Major comments:

Although the authors claim that the interaction between the uterus and embryo is crucial for egg-cylinder formation, they did not utilize uterus-derived cells nor analyze these. They just observed how blastocysts grow autonomously into the egg-cylinder shape in the hydrogel which has solely physical properties of the uterus but not biochemical features except for the RGD peptide-mediated cell adhesion process. Thus, it is still uncertain if similar mechanisms contribute to egg-cylinder formation in utero. To fulfill the gap between ex vivo morphogenesis and in utero, the authors would be expected to analyze the interaction between trophoblast and uterus in utero if uterine mechanisms can follow the integrin-mediated adhesion and a droplet wetting process. For example, whether integrin can contribute to egg-cylinder formation in utero can be proved by analyzing knock-out phenotypes of integrin-related genes. It will take around six months to conduct such suggested experiments. Otherwise, the authors should modify their statement "the interaction between embryo and uterine" into "the interaction between embryos and uterine-like hydrogels" throughout the manuscript.

Specific point:

Supplemental figure 1h, page 4 lines 20-23: The authors claim that 1.5-2 % PEG generated the shear modulus at 100-300 Pa, which is in the stiffness range of the E5.5 mouse decidua (Govindasamy et al., 2021). In Govindasamy's paper, elasticity measurements were performed in Petri dishes using an MFP-3D Classic AFM (Asylum Research, Wiesbaden, Germany) and cantilevers with a force constant of 0.08 with spherical tips (2 mm; NanoWorld, Neuchatel, Switzerland). In the present paper, the shear modulus (G′) of hydrogels was determined by performing small-strain oscillatory shear measurements on a Bohlin CVO 120 rheometer with plate-plate geometry. Therefore, it is not appropriate that Govindasamy's modulus is compared to the authors' modulus directly. For a direct comparison of the two modulus values, the authors can measure the stiffness of PEG with AFM or the shear modulus of the E5.5 mouse decidua by their rheometer.

Significance

Strong points:

As described in summary, the authors have newly identified that integrin-mediated adhesion between trophoblast and matrix facilitates egg-cylinder shape and the interaction between embryos and hydrogels is followed by a droplet-wetting process. These findings are considered to be novel by their excellent ex vivo imaging method.

Limitations:

It remains unaddressed that ex vivo mechanisms they have identified contribute to the egg-cylinder formation in utero.

Audience:

The results demonstrated here by the authors are fascinating in terms of general interest after the above concerns are appropriately addressed.

Since I am an experimental biologist, I don't have sufficient expertise to assess if the physical droplet model can recapitulate the interaction of the embryo and pre-patterned hydrogel for egg cylinder formation in detail.

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Reply to the reviewers

We thank all the Reviewers for their highly constructive reviews. Below, I have pasted the Reviewer’s comments in black and my replies in red, for easy reading.

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

In their study, Zhu and colleagues study how the centrosome proteins Spd-2 and Cnn in Drosophila recruit gamma-tubulin complexes to centrosomes, which is an important step in mitotic spindle formation. The authors make use of mutant flies and RNAi and find that the two factors Spd-2 and Cnn together are responsible for mitotic centrosomal accumulation of gamma-tubulin. By inactivating Spd-2 or Cnn separately, the authors show that Cnn appears to recruit the large share of mitotic gamma-tubulin pool by its CM1-domain. Interestingly, this involves only gamma-TuSCs (subcomplexes of gamma-TuRC) and not gamma-TuRCs. A smaller pool is recruited by Spd-2, and this pool depends on gamma-tubulin complex proteins that are only present in pre-assembled, complete gamma-TuRCs. This suggests that Drosophila makes microtubule nucleation templates in two ways. First, as in yeast, by direct recruitment of gamma-TuSCs to mitotic centrosomes, where additionally oligomerization needs to happen. And second, by recruitment and activation of preassembled gamma-TuRCs. Inactivation of both Cnn- and Spd-2 pathways abolishes mitosis-specific gamma-tubulin recruitment, resulting in low, but not complete loss of gamma-tubulin at centrosomes. The authors show that these low-gamma-tubulin centrosomes are still able to organize microtubules, but these microtubules have different dynamicity. Inspired by existing literature in flies and other model organisms, the authors identify Msps/Xmap215 as an important nucleation factor in this scenario.

Major points:

1) The authors use fly embryos with mutant Grip71, Grip75 and Grip163 alleles, which are central to the study. Most conclusions are based on the assumption that some mutants contain only gamma-TuSC, whereas wildtype cells contain a mix of gamma-TuSC and gamma-TuRC. It would be important to show sucrose gradient analyses of extracts to confirm the expected presence/absence of gamma-TuSC/gamma-TuRC.

We agree that it would be nice to perform sucrose gradient analysis of γ-tubulin mutants in different mutant backgrounds, but unfortunately this is not as easy as the Reviewer may think. To clarify, we have used larval brain cells (not embryos) for the analysis of γ-tubulin recruitment to centrosomes. We cannot use embryos because most mutant combinations are lethal beyond larval stages, meaning that mutant adult females are not available for embryo collection (embryos use maternally loaded proteins and mRNA and so it is the genotype of the mother that is important). Performing sucrose gradients with larval brain extracts would be extremely challenging, if not impossible, because a relatively large amount of starting material is required for sucrose gradient centrifugation, and manually dissecting and preparing hundreds if not thousands of larval brains is unrealistic, especially as mutant larvae are rare.

Given that we are not able to carry out these experiments, we have modified the text to include the caveat that some higher-order complexes may partially form in certain mutants. For example, in relation to the ability of Grip71 to recruit γ-TuSCs in cnn,grip75,grip163 mutants, the text now reads: “Thus, Spd-2 appears to recruit a very small amount of γ-TuSCs (which may, or may not, be present as larger assemblies due to an association with Grip128-γ-tubulin) via Grip71 (i.e. the recruitment that occurs in cnn,grip75GCP4,grip163 GCP6 cells), but its recruitment of γ-tubulin complexes relies predominantly on the GCP4/5/4/6 core.”

Nevertheless, the most important conclusion is that Cnn can recruit γ-TuSCs independent of pre-formed cytosolic γ-TuRCs and this is based on the finding from one particular mutant – the spd-2,grip71,grip75,grip128,grip163 mutant – where γ-tubulin levels at mitotic centrosomes are only very slightly reduced compared to single spd-2 mutants (Figure 1B). This conclusion is based on three assumptions that we argue are all very reasonable:

Assumption 1: flies depleted of 2, if not all 3, GCP4/5/4/6 core components (grip75,grip128,grip163) do not have a functioning GCP4/5/4/6 core. The Grip75GCP4 allele is a null mutant and is combined with a deficiency chromosome that depletes the whole Grip75GCP4 gene, and the Grip163GCP6 allele is a very strong depletion allele and is also combined with a deficiency chromosome that depletes the whole Grip163GCP6 gene. Even if the efficiency of the RNAi against Grip128GCP5 were poor, it would be hard to form a GCP4/5/4/6 core without Grip75GCP4 and in the near absence of Grip163GCP6 (which together provide 3 of the 4 molecules of the complex, including the outermost ones).

Assumption 2: cells depleted of the GCP4/5/4/6 core cannot assemble cytosolic γ-TuRCs. This is reasonable given that even individual depletion of Grip75GCP4, Grip128GCP5 or Grip163GCP6 already strongly reduces the presence of cytosolic γ-TuRCs (Vogt et al., 2006; Vérollet et al., 2006). In spd-2,grip71,grip75,grip128,grip163 mutant brain cells, the only γ-TuRC protein not targeted, except for the γ-TuSC components, is Actin (Mozart 1 is expressed only in testes (Tovey et al., 2018) and Mzt2 does not exist in flies). In Xenopus and humans, Actin appears to facilitate γ-TuRC assembly via interactions with a GCP6-N-term-Mzt1 module, and so it would be unlikely to allow γ-TuSC assembly into higher-order complexes without GCP6 (i.e Grip163GCP6) and Mzt1.

Assumption 3: Were Cnn not able to recruit γ-TuSCs independently of pre-formed γ-TuRCs, we would expect a much stronger reduction in γ-tubulin recruitment to centrosomes in spd-2,grip71,grip75,grip128,grip163 mutant cells. It is reasonable to assume, even without sucrose gradients, that the assembly of γ-TuRCs is strongly impeded in spd-2,grip71,grip75,grip128,grip163 mutant cells. Nevertheless, γ-tubulin is still recruited to centrosomes at ~66% compared to ~77% in spd-2 single mutant cells. While statistically significant (as stated in the updated manuscript), this reduction would surely be much greater were Cnn not able to recruit γ-TuSCs.

In the absence of experimental data, we have therefore made these arguments in the main text by making some text modifications and adding a new paragraph, as follows:

*“….the centrosomes in spd-2,grip71,grip75GCP4,grip128GCP5-RNAi,grip163GCP6 mutant cells had ~66% of the γ-tubulin levels found at wild-type centrosomes, only slightly lower than ~77% in spd-2 mutants alone (Figure 1A,B). Thus, the recruitment of γ-tubulin to mitotic centrosomes that occurs in the absence of Spd-2, i.e. that depends upon Cnn, does not appear to require Grip71 or the GCP4/5/4/6 core. *

While we cannot rule out that residual amounts of GCP4/5/4/6 core components in spd-2,grip71,grip75GCP4,grip128GCP5-RNAi,grip163GCP6 mutant cells may support a certain level of γ-TuSC oligomerisation in the cytosol, we favour the conclusion that Cnn can recruit γ-TuSCs directly to centrosomes in the absence of the GCP4/5/4/6 core for several reasons: First, the alleles used for grip71 and grip75GCP4 are null mutants, and the allele for grip163GCP6 is a severe depletion allele (see Methods), and even individual mutations in, or RNAi-directed depletion of, Grip75GCP4, Grip128GCP5 or Grip163GCP6 are sufficient to strongly reduce the presence cytosolic γ-TuRCs (Vogt et al., 2006; Vérollet et al., 2006). Second, spd-2,grip71,grip75GCP4,grip128GCP5-RNAi,grip163GCP6 mutant cells are depleted for all structural γ-TuRC components except for γ-TuSCs and Actin (note that Mozart1 (Mzt1) is not expressed in larval brain cells (Tovey et al., 2018) and that Mzt2 does not exist in flies). In human and Xenopus γ-TuRCs, Actin supports γ-TuRC assembly via interactions with a GCP6-N-term-Mzt1 module (Liu et al., 2019; Wieczorek et al., 2019, 2020; Zimmermann et al., 2020; Consolati et al., 2020), and so Actin alone is unlikely to facilitate assembly of γ-TuSCs into higher order structures. Third, our data agree with the observation that near complete depletion of Grip71, Grip75GCP4, Grip128 GCP5, and Grip163GCP6 from S2 cells does not prevent γ-tubulin recruitment to centrosomes (Vérollet et al., 2006). Fourth, given the strength of mutant alleles used, one would have expected a much larger decrease in centrosomal γ-tubulin levels in spd-2,grip71,grip75GCP4,grip128GCP5-RNAi,grip163GCP6 mutant cells were Cnn not able to directly recruit γ-TuSCs to centrosomes. Thus, our finding that Cnn can still robustly recruit γ-tubulin to centrosomes in spd-2,grip71,grip75GCP4,grip128GCP5-RNAi,grip163GCP6 mutant cells strongly suggests that Cnn can recruit γ-TuSCs to centrosomes without a requirement for them to first assemble into higher-order complexes.”

2) Given the advantage of the CnnΔCM1 separation of function mutant, I do not understand why it is not used throughout the study. Instead, full Cnn loss is used, which results in strongly reduced Spd-2 levels (Figure 2C,D). Are the observed differences between wild-type and mutants in Figure 2-5 dependent on defective PCM or do they also occur in a CnnΔCM1 background?

This is a good point, and we agree that it would have been “cleaner” to use the CnnΔCM1 mutant in these experiments. The reason that the CnnΔCM1 mutant was not used is that this mutant allele was made only after we had already generated the multi-allele stocks and performed most of the other experiments in Figures 2-5. It would have taken a long time to go back and generate fly stocks containing the CnnΔCM1 allele instead of the cnn null mutant allele. As we have shown that the CnnΔCM1 mutant cannot recruit any γ-tubulin, we don’t believe that using this mutant would change the results regarding recruitment of γ-tubulin by the spd-2 pathway i.e. when we have examined γ-tubulin recruitment in the cnn mutant background (Figure 2). Nevertheless, in terms of the efficiency to which microtubules can be nucleated in the absence of γ-tubulin complexes, which was examined in a cnn,grip71,grip163 mutant background, it is likely that using a cnnΔCM1,grip71,grip163 mutant background would better maintain Spd-2 in the PCM and thus better allow Msps and Mei-38 to stimulate microtubule nucleation. We may therefore find that microtubules can be nucleated even more efficiently in the absence of γ-TuRCs. Note that we do state this caveat in the paper. That said, performing the experiments would not be essential to conclude that microtubules can be nucleated independent of γ-TuRCs, which is the main point of this part of the paper.

Should the Reviewer and Editor deem it necessary, we will generate CnnΔCM1,grip71,grip163 lines to test whether or not γ-tubulin can be recruited to mitotic centrosomes under these conditions, and, if no γ-tubulin is recruited, we will generate CnnΔCM1,grip71 ,grip163,Jup-mCherry lines to test the ability of these centrosomes to nucleate microtubules (using the CherryTemp). Please note, however, that this would be several months of difficult fly genetics and data collection and we would therefore appreciate it if you consider the cost/benefit ratio when making your decision on whether you expect this data or not.

3) Statistical tests should support the conclusions in the text. If the authors claim differences between different genetic backgrounds (e.g. that spd2-mutants only have ~77% of gamma-tubulin at mitotic centrosomes compared to wild-type), statistical tests must compare mutant mitosis vs. wild-type mitosis.

We agree. We have now carried out the appropriate statistical tests and included them in the new version of the paper. For more detail, see the response to Reviewer 2 point 2.

4) While Cnn, grip71, grip163 mutants do not accumulate gamma-tubulin at centrosomes in mitosis, they still have low levels of centrosomal gamma-tubulin. It is therefore misleading to refer to "gamma-tubulin negative centrosomes".

This is a fair point. While we suspect this small fraction of γ-tubulin is non-functional in regard to microtubule nucleation i.e. it is the interphase pool of γ-tubulin and interphase centrosomes do not organise microtubules, we agree that referring to them as "gamma-tubulin negative centrosomes" is misleading. We have now changed the text to refer to them simply as “cnn,grip71,grip163 mutant centrosomes” or “cnn,grip71,grip163 centrosomes”.

Minor points:

1) The abstract states that gamma-TuRC is a catalyst of microtubule nucleation. By definition, a catalyst takes part in a reaction but is not part of the final product. Although our knowledge of the nucleation mechanism is still incomplete, mechanistic studies suggest a non-catalytical mechanism since gamma-TuRC was found to stay attached to the microtubule end after nucleation (Consolati et al. 2020, Wieczorek et al. 2020).

We have now removed any reference to the γ-TuRC being a catalyst.

2) CnnΔCM1 flies: genotyping data should be provided besides describing gRNAs.

We are not entirely sure what the Reviewer means here. We had already stated in the main text and methods that the deletion region spanned from R98 to D167. For further clarity, we now included the word “inclusive” in both the main text and the methods: main text: “We therefore used CRISPR combined with homology-directed repair to delete the CM1 domain (amino acids 98-167, inclusive) from the endogenous cnn gene…”; Methods:“R98 to D167, inclusive”. Please do let us know if further information is required.

3) Is it important to combine spd-2 with all four mutants, grip75 grip128 grip163 and grip71? What about spd-2 grip71 cells and spd-2 grip75 grip128 grip163 cells? Should that not have the same effect?

This comment relates to Major point 1, as our main conclusion (that Cnn can recruit γ-TuSCs) is only possible when combining spd2 with all four mutants i.e. targetting all γ-TuRC specific proteins is the most likely way to deplete as many pre-formed γ-TuRCs as possible. Depleting only Spd-2 and Grip71 would leave fully assembled γ-TuRCs in the cytosol, as assembly does not require Grip71. Depleting Spd-2, Grip75, Grip128, and Grip163 would prevent cytosolic γ-TuRC assembly, but there is a possibility that Grip71 may still act as a link between γ-TuSCs and Cnn. It was therefore necessary to deplete Spd-2, Grip75, Grip128, and Grip163, and Grip71.

4) CM1-containing factors are the only known factors able to directly bind and activate gamma-TuRC. How do the authors envision activation of gamma-TuRC in the absence of Cnn?

This is a good question but remains unanswered. Phosphorylation of γ-TuRCs is the most obvious possibility. For example, Aurora A phosphorylates NEDD1 (homologue of Grip71) to promote microtubule nucleation (Pinyol et al., 2013). NME7 kinase has been shown to increase the activity of purified γ-TuRCs (Liu et al., 2014). Other γ-TuRC components are also phosphorylated, but the consequences on γ-TuRC activity are not known. Another possibility is that TOG proteins indirectly promote the closing of the γ-TuRCs while adding tubulin dimers onto γ-tubulin (Thawani et al., 2020).

5) Do the authors think that each identified pathway to microtubule nucleation (i.e. Spd-2/gamma-TuRC, Cnn/gamma-TuSC, Msps/mei38) as revealed by mutant genetic backgrounds contributes to a similar extent to overall nucleation capacity also in an unperturbed genetic background?

Another good question, but it is very difficult to answer. Our view is that when γ-TuRCs are present and active they will likely dominate microtubule nucleation, out-competing the ability of TOG domain proteins to stimulate microtubule nucleation independently of γ-TuRCs. Nevertheless, TOG proteins will likely help promote microtubule nucleation from γ-TuRCs when both are present, as has been previously shown in vitro (Thawani et al., 2018; King et al., 2020; Consolati et al., 2020) and in fission yeast (Flor-Parra et al., 2018). We also believe that both Spd-2 and Cnn γ-TuRC recruitment pathways will contribute simultaneously. Another question is whether Cnn recruits γ-TuRCs instead of γ-TuSCs when γ-TuRCs are present in the cytosol. We assume this will depend on Cnn’s affinity of γ-TuRCs versus γ-TuSCs and on the relative levels of γ-TuRCs and γ-TuSCs in the cytosol.

6) How does CM1 mediate binding to gamma-TuRC? Using recombinant Cnn fragments, the authors find that a Cnn triple mutant (R101Q, E102A and F115A) no longer binds gamma-tubulin, suggesting these residues together mediate binding to gamma-tubulin complexes. However, it is not tested to what extent R101, E102 and F115 individually contribute to gamma-tubulin binding. Does the binding mode in Drosophila resemble more the one in humans or in budding yeast? Also, was this done with extracts from Grip71, Grip75, Grip128RNAi, Grip163 embryos or normal embryos?

In future, we will test the relative contributions of R101, E102 and F115, but for this study we wanted only to show that the CM1 domain was necessary for Cnn binding (hence why we directly mutated all three residues). We apologise for not stating that the IPs were carried out using wild-type embryos extracts – we have now included this information in the main text and methods.

7) Figure 2C: Should the green channel not correspond to Spd-2?

Thank you for pointing out this mistake – now corrected.

8) I suggest to reconsider the color-coding of graphs. While the colored background of the dot plots in Figure 1 and 2 are a matter of taste, the coloring of graphs in Figure 4F-H is confusing. Here, genetic backgrounds of fly lines are colored in the same way as the microscopy channels in Figure 4A-E, but they do not belong together.

We have now modified the colour-coding of images/graphs in Figure 4A-E as suggested.

9) A tacc mutant allele is used in experiments, but is not further described. Please provide the necessary background information.

We thank the reviewer for pointing this out. We had also forgotten to include the msps alleles used. The information for msps and tacc are now included in the methods.

10) The authors assess spindle quality in Cnn, grip71, grip163 cells and show that spindle quality worsens with ectopic msps. For comparison it would be good to compare spindle quality side by side with a wild-type situation.

This data is now included in Figure S4A,B.

11) Introduction: "[...], however, as they depend upon each other for their proper localisation within the PCM and act redundantly." - Sentence is incomplete.

I think this was just to do with how we had phased the sentence (the position of “however” was confusing). We have now rephrased the sentence: “It is complicated, however, to interpret the individual role of these proteins in the recruitment of γ-tubulin complexes, as they depend upon each other for their proper localisation within the PCM and act redundantly”.

12) Introduction: "Cnn contains the highly conserved CM1 domain (Sawin et al., 2004), which binds directly to γ-tubulin complexes in yeast and humans (Brilot et al., 2021; Wieczorek et al., 2019)". - Choi et al 2010 should also be cited here.

This citation has been added.

13) Results: "Typically, interphase centrosomes have only ~5-20% of the γ-tubulin levels found at mitotic centrosomes, [...]". - Citation is needed

We now cite our Conduit et al., 2014 paper.

14) The authors should discuss that Msps was found to act non-redundantly with gamma-tubulin in interphase nucleation (Rogers, MBC, 2008), contrary to the conclusions in the current manuscript.

Thank you for pointing this out. We have now modified the relevant part of the discussion to read:

“TOG domain and TPX2 proteins have been shown to work together with γ-TuRCs (or microtubule seed templates) to promote microtubule nucleation (Thawani et al., 2018; Flor-Parra et al., 2018; Gunzelmann et al., 2018b; Consolati et al., 2020; King et al., 2020; Wieczorek et al., 2015). Consistent with this, co-depletion of γ-tubulin and the Drosophila TOG domain protein Msps did not delay non-centrosomal microtubule regrowth after cooling compared to single depletions in interphase S2 cells (Rogers et al., 2008). Nevertheless, several studies, mainly in vitro, have shown that TOG and TPX2 proteins can also function independently of γ-TuRCs to promote microtubule nucleation (Roostalu et al., 2015; Woodruff et al., 2017; Schatz et al., 2003; Slep and Vale, 2007; Ghosh et al., 2013; Thawani et al., 2018; King et al., 2020; Zheng et al., 2020; Tsuchiya and Goshima, 2021; Imasaki et al., 2022). Our data suggest that, unlike from non-centrosomal sites in interphase S2 cells, Msps can promote γ-TuRC-independent microtubule nucleation from centrosomes in mitotic larval brain cells. This difference may reflect the ability of centrosomes to concentrate Msps at a single location.”

**Referees cross-commenting**

This is a good paper in my opinion, they need to add some controls though, to determine the expected presence/absence of gTuSC/gTuRC in the different mutants. An important advance is the finding that gTuSC can function as nucleator in parallel to gTuRC, depending on the recruitment mechanism. Different recruitment mechanisms, nucleation templates, and regulatory strategies co-exist and provide complex regulation and robustness to nucleation/spindle assembly. We thank the Reviewer for their thorough and constructive review. We hope they will agree to allow publication without us having to perform the sucrose gradient experiments that, as discussed above, will be very difficult, if not impossible, to carry out.

Reviewer #1 (Significance (Required)):

This is a very well-executed study and the data is presented clearly. However, some findings would benefit from additional experiments to substantiate the main interpretations. If these points are addressed, the study would provide an important conceptual advance in the field, namely that animal cells may rely on two different gamma-tubulin complexes for nucleation at mitotic centrosomes, gamma-TuSC and gamma-TuRC, which differ not only in their composition of GCP proteins but also the mode of recruitment to the centrosome. The findings will be of interest to all cell biologists.

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

Summary This paper sets out to further our understanding of how two proteins, Cnn and Spd-2, independently recruit g-Tubulin ring complexes(g-TuRC) to mitotic centrosomes in Drosophila cells. It uses some robust classical genetics to generate mutants to reduce/remove GCP4/5/6, Dgrip71 and Cnn and Spd-2 from cells, monitoring the consequences using live imaging.

It begins by showing that Cnn can recruit g-Tubulin independently of the core g-TuRC components or Dgrip71, and that a mutant Cnn lacking the CM1 domain cannot, strongly suggesting that, similarly to other organisms, the CM1 domain is essential for this function.

It then demonstrates that Spd-2, in contrast, cannot localise g-Tubulin in the absence of the g-TuRC components or Dgrip71.

In the second half of the paper, then use this tool as a proxy for centrosomes that completely lack mitotic g-Tubulin recruitment, in order to explore spindle assembly in the absence of centrosomal g-Tubulin. The show that microtubules and spindle are still nucleated but do so with different dynamics. This section is particularly convincing, given the use of the live de/repolymerisation assays using the CherryTemp device.

Finally, the authors visualise spindle formation in the absence of centrosomal g-Tubulin, alongside a number of other MT associated proteins, including Msps.

Major Comments 1. The claims and conclusions relating to the first half of the paper are supported by the data, but they need to be caveated by a clear explanation of the alleles used. Some are well-characterised mutant lines but have they been previously shown to completely remove the associated protein products? For the RNAi lines, do the authors have evidence (via Western blots) that these remove the protein products? It is not necessary that they show Western blots for all the lines, and it does not invalidate the major conclusions that the fly line carrying mutations in cnn, grip71, grip163 completely fails to localise g-Tubulin to mitotic centrosomes. However, they need to help the reader understand much more clearly whether these lines are complete nulls and, consequently this may impact the strength of their interpretation of the relationship between Grip163 versus Grip75, discussed both at the end of the relevant section and in the Discussion.

We appreciate the reviewer’s concern and have now included a detailed description in the Methods section of the alleles we use and their known effect on protein levels (pasted below for convenience). We have also included western blots for cnn and spd2 mutants to show the absence of detectable protein in larval brains. Unfortunately, we could not provide western blots for the other mutants, as we don’t have working antibodies for these proteins (although for Grip71 we did make an antibody and did western blots that showed the absence of protein in grip71 mutants, but this antibody has now been commercialised and so the western blot is published on the CRB website: https://crbdiscovery.com/polyclonal-antibodies/anti-grip71-antibody/). Nevertheless, protein levels for the grip75, grip163, msps and tacc mutants have been shown previously (now cited in the new text). We have also modified the main text to allow the reader to better understand whether proteins are completely absent or strongly reduced. In response to the specific comment about interpreting the relationship between Grip163 and Grip75, as we mention in the new methods section, the Grip75 allele is a null mutant while the Grip163 mutant is a severe depletion; thus, the fact that the Grip163 mutant has a stronger effect on γ-tubulin recruitment is not due to a stronger depletion.

New text in methods: “For spd-2 mutants, we used the dspd-2Z35711 mutant allele, which carries an early stop codon resulting in a predicted 56aa protein. Homozygous dspd-2Z35711 mutant flies lack detectable Spd-2 protein on western blots and so the allele is therefore considered to be a null mutant (Giansanti et al., 2008). This allele no longer produces homozygous flies (which is common for mutant alleles kept as balanced stocks for many years), which combined dspd-2Z35711 with a deficiency that includes the entire spd-2 gene (dspd-2Df(3L)st-j7). On western blots, there was no detectable Spd-2 protein in extracts from dspd-2Z35711 / dspd-2Df(3L)st-j7 hemizygous mutant brains (Figure S4B). For cnn mutants, we combined the cnnf04547 and cnnHK21 mutant alleles. The cnnf04547 allele carries a piggyBac insertion in the middle of the cnn gene and is predicted to disrupt long Cnn isoforms, including the centrosomal isoform (Cnn-C or Cnn-PA) (Lucas and Raff, 2007). This mutation is considered to be a null mutant for the long Cnn isoforms (Lucas and Raff, 2007; Conduit et al., 2014). The cnnHK21 allele carries an early stop codon after Cnn-C’s Q78 (Vaizel-Ohayon and Schejter, 1999) and affects both long and short Cnn isoforms – it is considered to be a null mutant (Eisman et al., 2009; Chen et al., 2017a). On western blots, there was no detectable Cnn-C protein in cnnf04547 / cnnHK21 hemizygous mutant brains (Figure S4A). For Grip71, we used the grip71120 mutant allele, which is a result of an imprecise p-element excision event that led to the removal of the entire grip71 coding sequence except for the last 12bp; it is considered to be a null mutant (Reschen et al., 2012). We combined this with an allele carrying a deficiency that includes the entire grip71 gene (grip71Df(2L)Exel6041). On western blots, there is no detectable Grip71 protein in grip71120 / grip71df6041 hemizygous mutant brains (see blots on CRB website, which were performed by us). For Grip75GCP4, we used the grip75175 mutant allele, which carries an early stop codon after Q291. Homozygous grip75175 mutant flies lack detectable Grip75GCP4 protein on western blots and so the allele is therefore considered to be a null mutant (Schnorrer et al., 2002). We combined this with an allele carrying a deficiency that includes the entire grip75GCP4 gene (grip75Df(2L)Exel7048). In the absence of a working antibody, we have not confirmed the expected absence of Grip75GCP4 protein in grip75175 / grip75Df(2L)Exel7048 hemizygous mutant flies on western blots. For Grip128GCP5, we used the UAS-controlled grip128-RNAiV29074 RNAi line, which is part of the VDRC’s GD collection, and drove its expression using the Insc-Gal4 driver (BL8751), which is expressed in larval neuroblasts and their progeny. In the absence of a working antibody, we have not confirmed the absence or reduction of Grip128GCP5 protein on western blots. RNAi was used for grip128GCP5 as its position on the X chromosome made generating stocks with multiple alleles technically challenging. For Grip163GCP6, we used the grip163GE2708 mutant allele, which carries a p-element insertion between amino acids 822 and 823 (total protein length is 1351aa) and behaves as a null or strong hypomorph mutant (Vérollet et al., 2006). We combined this with an allele carrying a deficiency that includes the entire grip163GCP6 gene (grip163Df(3L)Exel6115). In the absence of a working antibody, we have not confirmed the absence or reduction of Grip163GCP6 protein in grip163GE2708 / grip163Df(3L)Exel6115 hemizygous mutant flies on western blots. For Msps, we used the mspsp and mspsMJ15 mutant alleles. The mspsp allele carries a p-element insertion within, or close to, the 5’ UTR of the msps gene and results in a strong reduction, but not elimination, of Msps protein on western blots (Cullen et al., 1999). The mspsMJ15 allele was generated by re-mobilisation of the p-element (the genetic consequence of which has not been defined) and also results in a strong reduction, but not elimination, of Msps protein on western blots (Cullen et al., 1999; Lee et al., 2001). For TACC, we used the taccstella allele which contain a p-element insertion of unknown localisation but that results in no detectable TACC protein on western blots (Barros et al., 2005). For Mei-38, we used the UAS-controlled mei-38-RNAiHMJ23752 RNAi line, which is part of the NIG’s TRiP Valium 20 collection, and drove its expression using the Insc-Gal4 driver (BL8751). In the absence of a working antibody, we have not confirmed the absence or reduction of Mei-38 protein on western blots. RNAi was used for mei-38 as its position on the X chromosome made generating stocks with multiple alleles technically challenging. Moreover, the only available mutant of mei-38 affects a neighbouring gene.”

I have an issue with the statistics in Figure 1 &2. I realise the t-tests in Figure 1 show the significant differences between g-Tubulin recruitment to centrosomes in interphase and mitosis, in order to demonstrate the difference between the Spd-2;Grip combination line in (B) and the Spd-2; CnnCM1 double mutant in (D). But in doing so, it draws attention to the fact that there is no similar t-test between mitotic g-Tubulin recruitment to centrosomes in WT, Spd-2 and the Spd-2;Grip combination lines. This lack of stats between conditions is further confused by the language used in the text: In the Figure legend, the authors claim mitotic centrosomal g-Tubulin levels between are WT, Spd-2 and the Spd-2;Grip combination lines "similar", and in the text they say: the spd-2 Grip combination line had g-Tubulin "similar to the levels found at spd-2 mutants alone". But then they give numbers - an average of 77% of wild type for spd2 and 66% of wild type for the spd-2 Grip combination. I'm sure if they did a t-test they would find a significant difference between these conditions. This doesn't invalidate the thrust of what they're claiming, but they do need to be consistent in language, analysis and interpretation.

We agree that we should have performed a statistical comparison between the γ-tubulin levels for “WT mitosis” vs “spd2 mitosis” and for “spd-2 mitosis” vs “spd2,grip71,grip75,grip128,grip163 mitosis” (Figure 1B). We have now done this and found statistically significant differences in both cases. We have included the new p-values in the figure and modified the main text to read: “In fact, the centrosomes in these spd-2,grip71,grip75GCP4,grip128GCP5-RNAi,grip163GCP6 mutant cells had ~66% of the γ-tubulin levels found at wild-type centrosomes, only slightly lower than the levels found at spd-2 mutants alone (Figure 1A,B).”; and we have modified the legend to read: “A one-way ANOVA with a Sidak’s multiple comparisons test was used to make the comparisons indicated by p values in the graph. Note that there is only a small reduction in mitotic centrosomal γ-tubulin levels in spd-2 mutants and in spd-2, grip71,grip75GCP4, grip128GCP5-RNAi,grip163GCP6 mutants, showing that Cnn can still efficiently recruit γ-tubulin complexes to mitotic centrosomes when only γ-TuSCs are present.” Note that due to performing comparisons multiple times with the same data sets, it was necessary to use a one-way ANOVA with a Sidak’s multiple comparisons test (rather than paired t-tests).

For Figure 1D, we did not compare WT mitosis vs cnn∆CM1,spd-2 mitosis, as the point here was to test whether there was an increase from interphase to mitosis in cnn∆CM1,spd-2 mutants and we wanted to maintain the statistical power of using a paired t-test (one is more likely to detect differences with a paired t-test than with a multiple comparisons ANOVA, making the conclusion that there is no difference between interphase and mitotic cnn∆CM1,spd-2 centrosomes even more solid).

Similarly, in Figure 2, it would be better to assess any statistically significant difference between mitotic accumulation of g-Tubulin between fly lines, rather than accumulation between interphase and mitosis (which is pretty clear cut). This would help to clarify whether differences between loss of grip subunits are merely additive or synergistic. Again, this doesn't invalidate the overall result that concomitant loss of cnn, grip71 and grip163 completely abolishes mitotic centrosomal accumulation of g-Tubulin, but it is a more complete analysis of the extant data.

As for Figure 2, we respectfully disagree that we should make comparisons between genotypes instead of, or in addition to, making comparisons between interphase and mitotic centrosomes within the same genotype. This is because we will lose statistical power by performing a multiple comparisons test. Indeed, if we were to compare both within and between selected genotypes (14 comparisons in total), then we lose the statistically significant differences between interphase and mitotic centrosomes in cnn,grip75,grip163 (p=0.04) and cnn,grip71,grip75 (p=0.08) genotypes, when there clearly appears to be a difference (as stated by the Reviewer). Given that the point of this experiment is to elucidate which proteins are required to allow maturation from interphase to mitosis, rather than which combination of mutations has the stronger effect, we feel that maintaining the paired t-test analysis is more appropriate.

One OPTIONAL experiment that would significantly improve the study would be similar CherryTemp live imaging of the cells lacking both centrosomal g-Tubulin and Msps. Currently the manuscript finishes with a fixed analysis of MT de/repolymerisation in these cells, which provides evidence that Msps has a role in MT nucleation in the absence of centrosomal g-Tubulin-nucleated MTs, but very little else can be concluded.

We would love to do this experiment but the genetics are complicated. We would have to generate stocks containing a cnn,grip71,GFP-PACT triple allele chromosome II and a grip163,msps,Jupiter-mCherry triple allele chromosome III. While live data would provide interesting insights into the dynamics of microtubules nucleated in the absence of γ-TuRCs and reduction of Msps, our fixed analysis is at least sufficient to implicate Msps in γ-TuRC-independent microtubule organisation.

1. There is, perhaps surprisingly, no mention of Augmin in the paper. Augmin has been shown to recruit g-TuRC to pre-existing MTs, through the grip71 subunit (Chen et al., 2017). So, presumably, in cnn, grip71, grip163, g-Tubulin cannot be recruited to pre-existing MTs either? This could add impact to the results - in that it implies the MT nucleation seen in the absence of cnn, grip71 and grip163 actually reflects, not just loss of centrosome function, but also loss of Augmin function. Mentioning this in the discussion could help increase the impact of the paper.

We apologise for this oversight. Indeed, it is perfectly possible that Grip71/Augmin-mediated amplification of microtubules during microtubule re-growth from centrosomes could influence the difference in recovery rates between control and mutant centrosomes. We have now modified the results section to read:

“Our data suggest that microtubules are more resistant to cold-induced depolymerisation when they have been nucleated independently of γ-TuRCs, but that microtubules are nucleated more efficiently when γ-TuRCs are present. However, it must be considered that, due to the loss of Cnn from centrosomes in the cnn,grip71,grip163 mutant cells, general PCM levels are reduced, likely reducing the levels of any protein involved in γ-TuRC-independent microtubule nucleation. Moreover, Grip71 is necessary for γ-TuRC recruitment to microtubules, most likely via the Augmin complex (Reschen et al., 2012; Chen et al., 2017b; Dobbelaere et al., 2008; Vérollet et al., 2006), enabling microtubules to be nucleated from the sides of pre-existing microtubules. Thus, the potential for Augmin-mediated amplification of centrosome-nucleated microtubules in control cells may also contribute to the increased microtubule recovery speed in control cells. Importantly, however, both of these caveats make it even clearer that microtubules can be nucleated independently of γ-TuRCs from mitotic centrosomes in Drosophila.”

Minor comments 1. The cnn, grip71, grip163 mutant image in Fig3 B after 40 min cooling appears to have 4 centrioles. Is this a cell that exited and re-entered mitosis?

Cnn mutant cells often have centrosome segregation problems, resulting in cells with variable numbers of centrioles (Conduit et al., 2010b, Current Biology). We have now mentioned this in the legends for Figure 3, Figure 4, and Figure S4.

Methods should contain more detail on the de/repolymerisation live imaging analysis (including the numbers of cells contributing to the analysis) and techniques such exponential curve fitting.

We have now included this information in the methods and updated this information in the figure legend (to include cell numbers, not just centrosome numbers, and to indicate that GraphPad Prism was used to generate the models.

P5 para 2 - "GPC4/5/4/6" should read "GCP4/5/6"

We actually use the GCP4/5/4/6 nomenclature throughout as it represents the 2 copies of GCP4 to one copy of GCP5 and GCP6 in the complex, as well as the order of these molecules.

Fig legend 1 - "error bar" should read "scale bar"

Thanks, now corrected

Reviewer #2 (Significance (Required)):

The experimental approach (genetics and cell biology) taken in this manuscript is very appropriate and the experiments are of high quality. It uses the strengths of Drosophila to cleverly engineer flies to pull apart the relationship between two different ways to recruit the main MT nucleator, g-Tubulin, to mitotic centrosomes. This is an important advance for the specific research field of centrosome biology.

By generating a fly that completely fails to localise g-Tubulin to mitotic centrosomes, the paper is able to explore whether MTs and the mitotic spindle can form in its absence. Again, there is very high quality imaging and image analysis, using a commercially available (but very cool) fast heating/cooling apparatus - the CherryTemp to explore the dynamics of MT generation. The limitation to this approach, though, is that g-Tubulin itself is still present and presumably able to nucleate MTs in the cytosol or elsewhere, albeit inefficiently. As such, it adds to a body of centrosomal and cell division research, rather than adding a highly significant conceptual advance.

Similarly, the finding that Msps is involved in nucleating MTs in the absence of centrosomal g-Tubulin, via fixed analysis, supports other work, rather than moving the field forwards.

Overall, assuming the caveats mentioned in the major comments are dealt with, I see this as a robust and very well carried out piece of research, that will be of interest to those investigating the broad field of cell division

My field of expertise is Drosophila cell division

We thank the Reviewer for their thorough and constructive review. We hope that the reviewer may agree with us and the other Reviewers that revealing the complexity of γ-TuRC recruitment and microtubule nucleation at centrosomes, particularly the finding that different types of γ-tubulin complexes are recruited to centrosomes by different tethering proteins, provides an important conceptual advance.

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

Centrosomes are complex and it has been appreciated for some time that they likely nucleate microtubules by more than one mechanism. However, what these mechanisms exactly are, and which are the most significant has not been clear. A major contributor to centrosomal microtubule nucleation the tubulin isoform gamma-tubulin (g-tubulin), which is present in two complexes, a smaller gTuSC that contains gamma tubulin along with GCP2 and 3 and a larger g-tubulin ring complex (gTuRC) whose assembly additionally requires GCP4/5/6. A second high-level question has been whether the centrosome has any g-tubulin-independent microtubule nucleation mechanisms. In this manuscript, the authors use a collection of mutants and RNAi conditions in the Drosophila brain to generate a picture of centrosomal microtubule nucleation pathways. They show that there are two g-tubulin-dependent and a third g-tubulin-independent microtubule nucleation pathways. They show that the first g-tubulin-dependent pathway depends on the CM1 domain of the centrosomal PCM matrix protein, Centrosomin (Cnn) and on the gTuSC components GCP2/3, but not on the components specifically required for gTuRC assembly. The second g-tubulin-dependent pathway depends on Spd-2 (and not Cnn) and requires the gTuRC-specific components and NEDD1/Grip71. By inhibiting both of these pathways, the authors also show that there is a robust g-tubulin-independent microtubule nucleation pathway. Overall, has the potential to be an impactful contribution from a conceptual point-of-view. I would be excited to recommend publication if the major comments below, particularly points 1 and 2, could be addressed.

1. The experiment in Fig. 2B examines what is required for Spd-2 to recruit g-tubulin to mitotic centrosomes that lack Cnn. This panel should include a cnn mutant-only control, for which the readers are currently referred to an older paper from 2014. Without repeating this control in parallel to one of the conditions in this panel, it is impossible to say whether the addition of the grip71 mutation has any effect on g-tubulin levels.

This is a good point. We will perform a cnn vs cnn,grip71 experiment and include this data in the new version of the paper. This will take a couple of months, as this will involve growing up fly lines, performing the necessary crosses, microscopy, data analysis, and manuscript updating.

1. The experiment in Fig. 2B is in the background of a Cnn loss-of-function mutation in which centrosomal Spd-2 is at just under 40% of its levels in brains with Cnn (according to Fig. 2D). So the Spd-2 doing the recruiting-is the non-Cnn-dependent population. The authors should also do one experiment in the background of their Cnn-CM1delete mutant or their Cnn CM1 g-tubulin recruitment mutant, because these backgrounds would be expected to have normal amounts of Cnn matrix and normal levels of Spd-2. Comparing the amount of g-tubulin recruitment in a cnn loss-of-function mutant to that in a cnn-CM1delete mutant would reveal whether the Cnn-bound Spd-2 can contribute to g-tubulin recruitment in the same way that the Cnn-independent Spd-2 can. These two populations could easily differ in their ability to recruit g-tubulin. Also, is it clear that these two pathways can act in parallel (i.e. that assembly of the Cnn matrix around the centriole does not mask the ability of Cnn-independent Spd-2 to recruit g-tubulin)? Thus, there are three possibilities- all interesting- for the outcome of this experiment. The Cnn-CM1delete mutant/Cnn-CM1 g-tubulin recruitment mutants could: (1) recruit less g-tubulin than the cnn loss-of function mutant (if Cnn matrix assembly inhibits the Cnn-independent Spd-2 pathway), (2) recruit the same amount of g-tubulin as the cnn loss-of-function mutant (if the Cnn matrix does not inhibit the Cnn-independent Spd-2 pathway but Cnn-dependent Spd-2 does not itself recruit g-tubulin), or (3) recruit more g-tubulin than the cnn loss-of-function mutant (if both the Cnn-dependent and Cnn-independent Spd-2 can recruit g-tubulin).

These are very interesting points that we have not considered before. As the reviewer suggests, we will perform an analysis of γ-tubulin levels at centrosomes in cnnnull vs cnn∆CM1 to test the ability of Cnn-dependent and Cnn-independent populations of Spd-2 to recruit γ-tubulin. This should take ~2 months.

1. The paper needs a summary model figure that the field can understand. The current model in Fig. 2E does not suffice in this regard. It would be nice to have this model appear at the end of the paper to outline the 3 pathways for centrosomal microtubule nucleation outlined by the work. Maybe have an arc for the centrosome at the bottom of the figure and show arrows from the gTuSC to the Cnn CM1 domain from the gTuRC to the Cnn CM1 domain and the gTuRC to Spd-2 or something like this. How you draw this could be impacted by the experiment outlined above in point 2. Also, there would be a g-tubulin-independent pathway in the figure. Not everyone reads papers carefully, and you want people to be able to get the takeaway message at a glance.

We have now completely modified the Figure and moved it to the end of the paper (new Figure 5). We thank the Reviewer for this suggestion as it really does provide a clearer message for the reader.

1. The authors show that this pathway is modulated by loss of Minispindles (Msps)-but as this is a critical microtubule assembly factor, it seems likely that Msps loss might modulate all of the pathways. From the data in Figure 4, my main takeaway would be that Msps is not the central player in the g-tubulin independent nucleation pathway. It might make the paper more impactful to end the story after Fig. 4, move the current Fig. 5 to the supplement and add a nice model figure at the end.

We agree that Msps may play a role beyond microtubule nucleation, including plus end growth, and that this may also influence the efficiency of spindle formation in cnn,grip71,grip163,msps mutants. Nevertheless, our microtubule regrowth data in original Figure 5A clearly show that Msps is a key player in the g-tubulin independent nucleation pathway at centrosomes. Perhaps the Reviewer missed this point as the data was in Figure 5 and not Figure 4. Moreover, the original Figure 5E shows that the effect of depleting Msps in addition to cnn, grip71 and grip163 is specific to cells containing centrosomes i.e. if Msps played a significant role in microtubule regulation beyond its role at centrosomes, then one would expect spindle formation to be worse when comparing mutant cells that lack centrosomes. Nevertheless, we now realise it would be better to include the microtubule regrowth from centrosomes data for cnn,grip71,grip163 vs cnn,grip71,grip163,msps in Figure 4, and move the spindle assembly data from original Figure 5C-E to a new supplementary Figure (Figure S4). We then end the paper on a model figure in new Figure 5.

Minor comments: 5. In Fig. 1E the sequence labels are confusing. Please label each sequence on the left with the residue numbers in the corresponding endogenous protein that are shown in the alignment.

You are absolutely right, I’m not sure why our labelling was like that. Now corrected.

In Fig. 1F, please label with location of molecular weight markers

Now added.

Reviewer #3 (Significance (Required)):

Repeating my text from above. Centrosomes are complex and it has been appreciated for some time that they likely nucleate microtubules by more than one mechanism. However, what these mechanisms exactly are, and which are the most significant has not been clear. A major contributor to centrosomal microtubule nucleation the tubulin isoform gamma-tubulin (g-tubulin), which is present in two complexes, a smaller gTuSC that contains gamma tubulin along with GCP2 and 3 and a larger g-tubulin ring complex (gTuRC) whose assembly additionally requires GCP4/5/6. A second high-level question has been whether the centrosome has any g-tubulin-independent microtubule nucleation mechanisms. In this manuscript, the authors use a collection of mutants and RNAi conditions in the Drosophila brain to generate a picture of centrosomal microtubule nucleation pathways. They show that there are two g-tubulin-dependent and a third g-tubulin-independent microtubule nucleation pathways. They show that the first g-tubulin-dependent pathway depends on the CM1 domain of the centrosomal PCM matrix protein, Centrosomin (Cnn) and on the gTuSC components GCP2/3, but not on the components specifically required for gTuRC assembly. The second g-tubulin-dependent pathway depends on Spd-2 (and not Cnn) and requires the gTuRC-specific components and NEDD1/Grip71. By inhibiting both of these pathways, the authors also show that there is a robust g-tubulin-independent microtubule nucleation pathway. Overall, has the potential to be an impactful contribution from a conceptual point-of-view. I would be excited to recommend publication if the major comments, particularly points 1 and 2, could be addressed.

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Referee #3

Evidence, reproducibility and clarity

Centrosomes are complex and it has been appreciated for some time that they likely nucleate microtubules by more than one mechanism. However, what these mechanisms exactly are, and which are the most significant has not been clear. A major contributor to centrosomal microtubule nucleation the tubulin isoform gamma-tubulin (g-tubulin), which is present in two complexes, a smaller gTuSC that contains gamma tubulin along with GCP2 and 3 and a larger g-tubulin ring complex (gTuRC) whose assembly additionally requires GCP4/5/6. A second high-level question has been whether the centrosome has any g-tubulin-independent microtubule nucleation mechanisms. In this manuscript, the authors use a collection of mutants and RNAi conditions in the Drosophila brain to generate a picture of centrosomal microtubule nucleation pathways. They show that there are two g-tubulin-dependent and a third g-tubulin-independent microtubule nucleation pathways. They show that the first g-tubulin-dependent pathway depends on the CM1 domain of the centrosomal PCM matrix protein, Centrosomin (Cnn) and on the gTuSC components GCP2/3, but not on the components specifically required for gTuRC assembly. The second g-tubulin-dependent pathway depends on Spd-2 (and not Cnn) and requires the gTuRC-specific components and NEDD1/Grip71. By inhibiting both of these pathways, the authors also show that there is a robust g-tubulin-independent microtubule nucleation pathway. Overall, has the potential to be an impactful contribution from a conceptual point-of-view. I would be excited to recommend publication if the major comments below, particularly points 1 and 2, could be addressed.

1. The experiment in Fig. 2B examines what is required for Spd-2 to recruit g-tubulin to mitotic centrosomes that lack Cnn. This panel should include a cnn mutant-only control, for which the readers are currently referred to an older paper from 2014. Without repeating this control in parallel to one of the conditions in this panel, it is impossible to say whether the addition of the grip71 mutation has any effect on g-tubulin levels.
2. The experiment in Fig. 2B is in the background of a Cnn loss-of-function mutation in which centrosomal Spd-2 is at just under 40% of its levels in brains with Cnn (according to Fig. 2D). So the Spd-2 doing the recruiting-is the non-Cnn-dependent population. The authors should also do one experiment in the background of their Cnn-CM1delete mutant or their Cnn CM1 g-tubulin recruitment mutant, because these backgrounds would be expected to have normal amounts of Cnn matrix and normal levels of Spd-2. Comparing the amount of g-tubulin recruitment in a cnn loss-of-function mutant to that in a cnn-CM1delete mutant would reveal whether the Cnn-bound Spd-2 can contribute to g-tubulin recruitment in the same way that the Cnn-independent Spd-2 can. These two populations could easily differ in their ability to recruit g-tubulin. Also, is it clear that these two pathways can act in parallel (i.e. that assembly of the Cnn matrix around the centriole does not mask the ability of Cnn-independent Spd-2 to recruit g-tubulin)? Thus, there are three possibilities- all interesting- for the outcome of this experiment. The Cnn-CM1delete mutant/Cnn-CM1 g-tubulin recruitment mutants could: (1) recruit less g-tubulin than the cnn loss-of function mutant (if Cnn matrix assembly inhibits the Cnn-independent Spd-2 pathway), (2) recruit the same amount of g-tubulin as the cnn loss-of-function mutant (if the Cnn matrix does not inhibit the Cnn-independent Spd-2 pathway but Cnn-dependent Spd-2 does not itself recruit g-tubulin), or (3) recruit more g-tubulin than the cnn loss-of-function mutant (if both the Cnn-dependent and Cnn-independent Spd-2 can recruit g-tubulin).
3. The paper needs a summary model figure that the field can understand. The current model in Fig. 2E does not suffice in this regard. It would be nice to have this model appear at the end of the paper to outline the 3 pathways for centrosomal microtubule nucleation outlined by the work. Maybe have an arc for the centrosome at the bottom of the figure and show arrows from the gTuSC to the Cnn CM1 domain from the gTuRC to the Cnn CM1 domain and the gTuRC to Spd-2 or something like this. How you draw this could be impacted by the experiment outlined above in point 2. Also, there would be a g-tubulin-independent pathway in the figure. Not everyone reads papers carefully, and you want people to be able to get the takeaway message at a glance.
4. The authors show that this pathway is modulated by loss of Minispindles (Msps)-but as this is a critical microtubule assembly factor, it seems likely that Msps loss might modulate all of the pathways. From the data in Figure 4, my main takeaway would be that Msps is not the central player in the g-tubulin independent nucleation pathway. It might make the paper more impactful to end the story after Fig. 4, move the current Fig. 5 to the supplement and add a nice model figure at the end.

Minor comments:

1. In Fig. 1E the sequence labels are confusing. Please label each sequence on the left with the residue numbers in the corresponding endogenous protein that are shown in the alignment.
2. In Fig. 1F, please label with location of molecular weight markers

Significance

Repeating my text from above. Centrosomes are complex and it has been appreciated for some time that they likely nucleate microtubules by more than one mechanism. However, what these mechanisms exactly are, and which are the most significant has not been clear. A major contributor to centrosomal microtubule nucleation the tubulin isoform gamma-tubulin (g-tubulin), which is present in two complexes, a smaller gTuSC that contains gamma tubulin along with GCP2 and 3 and a larger g-tubulin ring complex (gTuRC) whose assembly additionally requires GCP4/5/6. A second high-level question has been whether the centrosome has any g-tubulin-independent microtubule nucleation mechanisms. In this manuscript, the authors use a collection of mutants and RNAi conditions in the Drosophila brain to generate a picture of centrosomal microtubule nucleation pathways. They show that there are two g-tubulin-dependent and a third g-tubulin-independent microtubule nucleation pathways. They show that the first g-tubulin-dependent pathway depends on the CM1 domain of the centrosomal PCM matrix protein, Centrosomin (Cnn) and on the gTuSC components GCP2/3, but not on the components specifically required for gTuRC assembly. The second g-tubulin-dependent pathway depends on Spd-2 (and not Cnn) and requires the gTuRC-specific components and NEDD1/Grip71. By inhibiting both of these pathways, the authors also show that there is a robust g-tubulin-independent microtubule nucleation pathway. Overall, has the potential to be an impactful contribution from a conceptual point-of-view. I would be excited to recommend publication if the major comments, particularly points 1 and 2, could be addressed.

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

Summary

This paper sets out to further our understanding of how two proteins, Cnn and Spd-2, independently recruit g-Tubulin ring complexes(g-TuRC) to mitotic centrosomes in Drosophila cells. It uses some robust classical genetics to generate mutants to reduce/remove GCP4/5/6, Dgrip71 and Cnn and Spd-2 from cells, monitoring the consequences using live imaging.

It begins by showing that Cnn can recruit g-Tubulin independently of the core g-TuRC components or Dgrip71, and that a mutant Cnn lacking the CM1 domain cannot, strongly suggesting that, similarly to other organisms, the CM1 domain is essential for this function.

It then demonstrates that Spd-2, in contrast, cannot localise g-Tubulin in the absence of the g-TuRC components or Dgrip71.

In the second half of the paper, then use this tool as a proxy for centrosomes that completely lack mitotic g-Tubulin recruitment, in order to explore spindle assembly in the absence of centrosomal g-Tubulin. The show that microtubules and spindle are still nucleated but do so with different dynamics. This section is particularly convincing, given the use of the live de/repolymerisation assays using the CherryTemp device.

Finally, the authors visualise spindle formation in the absence of centrosomal g-Tubulin, alongside a number of other MT associated proteins, including Msps.

Major Comments

1. The claims and conclusions relating to the first half of the paper are supported by the data, but they need to be caveated by a clear explanation of the alleles used. Some are well-characterised mutant lines but have they been previously shown to completely remove the associated protein products? For the RNAi lines, do the authors have evidence (via Western blots) that these remove the protein products? It is not necessary that they show Western blots for all the lines, and it does not invalidate the major conclusions that the fly line carrying mutations in cnn, grip71, grip163 completely fails to localise g-Tubulin to mitotic centrosomes. However, they need to help the reader understand much more clearly whether these lines are complete nulls and, consequently this may impact the strength of their interpretation of the relationship between Grip163 versus Grip75, discussed both at the end of the relevant section and in the Discussion.
2. I have an issue with the statistics in Figure 1 &2. I realise the t-tests in Figure 1 show the significant differences between g-Tubulin recruitment to centrosomes in interphase and mitosis, in order to demonstrate the difference between the Spd-2;Grip combination line in (B) and the Spd-2; CnnCM1 double mutant in (D). But in doing so, it draws attention to the fact that there is no similar t-test between mitotic g-Tubulin recruitment to centrosomes in WT, Spd-2 and the Spd-2;Grip combination lines. This lack of stats between conditions is further confused by the language used in the text: In the Figure legend, the authors claim mitotic centrosomal g-Tubulin levels between are WT, Spd-2 and the Spd-2;Grip combination lines "similar", and in the text they say: the spd-2 Grip combination line had g-Tubulin "similar to the levels found at spd-2 mutants alone". But then they give numbers - an average of 77% of wild type for spd2 and 66% of wild type for the spd-2 Grip combination. I'm sure if they did a t-test they would find a significant difference between these conditions. This doesn't invalidate the thrust of what they're claiming, but they do need to be consistent in language, analysis and interpretation. Similarly, in Figure 2, it would be better to assess any statistically significant difference between mitotic accumulation of g-Tubulin between fly lines, rather than accumulation between interphase and mitosis (which is pretty clear cut). This would help to clarify whether differences between loss of grip subunits are merely additive or synergistic. Again, this doesn't invalidate the overall result that concomitant loss of cnn, grip71 and grip163 completely abolishes mitotic centrosomal accumulation of g-Tubulin, but it is a more complete analysis of the extant data.
3. One OPTIONAL experiment that would significantly improve the study would be similar CherryTemp live imaging of the cells lacking both centrosomal g-Tubulin and Msps. Currently the manuscript finishes with a fixed analysis of MT de/repolymerisation in these cells, which provides evidence that Msps has a role in MT nucleation in the absence of centrosomal g-Tubulin-nucleated MTs, but very little else can be concluded.
4. There is, perhaps surprisingly, no mention of Augmin in the paper. Augmin has been shown to recruit g-TuRC to pre-existing MTs, through the grip71 subunit (Chen et al., 2017). So, presumably, in cnn, grip71, grip163, g-Tubulin cannot be recruited to pre-existing MTs either? This could add impact to the results - in that it implies the MT nucleation seen in the absence of cnn, grip71 and grip163 actually reflects, not just loss of centrosome function, but also loss of Augmin function. Mentioning this in the discussion could help increase the impact of the paper.

Minor comments

1. The cnn, grip71, grip163 mutant image in Fig3 B after 40 min cooling appears to have 4 centrioles. Is this a cell that exited and re-entered mitosis?
2. Methods should contain more detail on the de/repolymerisation live imaging analysis (including the numbers of cells contributing to the analysis) and techniques such exponential curve fitting.
3. P5 para 2 - "GPC4/5/4/6" should read "GCP4/5/6"
4. Fig legend 1 - "error bar" should read "scale bar"