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Referee #1

Evidence, reproducibility and clarity

The manuscript from Morh and collaborators reports the characterization of an ARF-like GTPase of Arabidopsis. Small GTPases of the ARF family play crucial role in intracellular trafficking and plant physiology. The ARF-like proteins are poorly addressed in Arabidopsis while they could reveal completely different function than the canonical known ARF proteins. Thus, the aim of the study is important and could be of interest to a wide range of plant scientists. I am impressed by the biochemical characterization of the TTN5 protein and its mutated versions, this is clearly a very nice point of the paper and allows for proper interpretations of the other results. However, I was much less convinced on the cell biology part of this manuscript and aside from the subcellular localization of the TTN5 I think the paper would benefit from a more functional angle. Below are my comments to improve the manuscript:

1. In the different pictures and movies, TTN5 is quite clearly appearing as a typical ER-like pattern. The pattern of localization further extends to dotty-like structures and structures labeled only at the periphery of the structure, with a depletion of fluorescence inside the structure. These observations raise several points. First, the ER pattern is never mentioned in the manuscript while I think it can be clearly observed. Given that the YFP-TTN5 construct is not functional (the mutant phenotype is not rescued) the ER-localization could be due to the retention at the ER due to quality control. The HA-TTN5 construct is functional but to me its localization shows a quite different pattern from the YFP version, I do not see the ER for example or the periphery-labeled structures. In this case, it will be a crucial point to perform co-localization experiments between HA-TTN5 and organelles markers to confirm that the functional TTN5 construct is labeling the Golgi and MVBs, as does the non-functional one. I am also quite sure that a co-localization between YFP-TTN5 and HA-TTN5 will not completely match... The ER is contacting so many organelles that the localization of YFP-TTN5 might not reflects the real location of the protein.
2. What are the structures with TTN5 fluorescence depleted at the center that appear in control conditions? They look different from the Golgi labeled by Man1 but similar to MVBs upon wortmannin treatment, except that in control conditions MVBs never appear like this. Are they related to any kind of vacuolar structures that would be involved in quality control-induced degradation of non-functional proteins?
3. The fluorescence at nucleus could be due to a proportion of YFP-TTN5 that is degraded and released free-GFP, a western-blot of the membrane fraction vs the cytosolic fraction could help solving this issue.
4. It is not so easy to conclude from the co-localization experiments. The confocal pictures are not always of high quality, some of them appear blurry. The Golgi localization looks convincing, but the BFA experiments are not that clear. The MVB localization is pretty convincing but the images are blurry. An issue is the quantification of the co-localizations. Several methods were employed but they do not provide consistent results. As for the object-based co-localization method, the authors employ in the text co-localization result either base on the % of YFP-labeled structures or the % of mCherry/mRFP-labeled structures, but the results are not going always in the same direction. For example, the proportion of YFP-TTN5 that co-localize with MVBs is not so different between WT and mutated version but the proportion of MVBs that co-localize with TTN5 is largely increased in the Q70L mutant. Thus it is quite difficult to interpret homogenously and in an unbiased way these results. Moreover, the results coming from the centroid-based method were presented in a table rather than a graph, I think here the authors wanted to hide the huge standard deviation of these results, what is the statistical meaning of these results?
5. The use of FM4-64 to address the vacuolar trafficking is a hazardous, FM4-64 allows the tracking of endocytosis but does not say anything on vacuolar degradation targeting and even less on the potential function of TTN5 in endosomal vacuolar targeting. Similarly, TTN5, even if localized at the Golgi, is not necessarily function in Golgi-trafficking.
6. The manuscript lacks in its present shape of functional evidences for a role of TTN5 in any trafficking steps. I understand that the KO mutant is lethal but what are the phenotypes of the Q70L and T30N mutant plants? What is the seedling phenotype, how are the Golgi and MVBs looking like in these mutants? Do the Q70L or T30N mutants perturbed the trafficking of any cargos?

Significance

In conclusion, I think this manuscript is a good biochemical description of an ARF-like protein but it would need to be strengthen on the cell biology and functional sides. Nonetheless, provided these limitations fixed, this manuscript would advance our knowledge of small GTPases in plants. The major conceptual advance of that study is to provide a non-canonical behavior of the active/inactive cycle dynamics for a small-GTPase. Of course this dynamic probably has an impact on TTN5 function and involvement in trafficking, although this remains to be fully demonstrated. Provided a substantial amount of additional experiments to support the claims of that study, this study could be of general interest for scientist working in the trafficking field.

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Reply to the reviewers

Compared to our initial submission to Review Commons, we have addressed all the reviewers' comments. We have extensively re-written the manuscript to make it clearer to a larger audience. In particular, we have transferred Figure EV1 to Figure 1 with more complete panels and included a scheme (Figure EV3) on the steps of D2R internalization which we measure with live cell imaging. We have added a new paragraph to the start of the Discussion to summarize our main conclusions and reordered the discussion on the possible mechanisms of membrane PUFA enrichment on D2R endocytosis. All the changes in the text are in red for easier comparison with the previous version.

As suggested by reviewer 1, we have performed additional experiments to test the specificity of the effects of PUFA treatments on D2R endocytosis, reinforcing the results shown in Figure 4 using feeding assays. We show with live cell TIRF imaging and the ppH assay that TfR-SEP endocytosis is not affected (Figure EV5) and that SEP-β2AR endocytosis and βarr2-mCherry recruitment to the plasma membrane are not affected (Figure EV6).

Reviewer #1

Evidence, reproducibility and clarity

*The manuscript, using different live and fixed cell trafficking assays, demonstrates that incorporation of poly-unsaturated, but not saturated, free fatty acids in the membrane phospholipids reduce agonist induced internalization of the D2 dopamine receptor but not the adrenergic beta2 receptors or the transferrin receptor. Pulsed pH (ppH) live microscopy further demonstrated that the reduced internalization by incorporation of free fatty acid was accompanied by a blunted recruitment of Beta-arrestin for the D2R.

I believe said claims put forward in the manuscript are overall well supported by the data and as such I do not believe that further experiments are necessarily needed to uphold these key claims. Also, the methodology is satisfactorily reported, and statistics are robust, although two-way Anova like used in Fig 1 seems appropriate for Fig 2 and 3*

We thank the reviewer for his/her positive assessment of our work. We have checked the statistical tests used for all our measures. For Figure 2 and 3 (now 3 and 4) we test for only one factor (PUFA treatment or not) so we ran ordinary one-way ANOVA using Graphpad Prism.

That said, I suggest that the fixed cell internalization experiments (Fig 2 and 3), which relate the effect on the D2R to B2AR and transferrin are revised. This is important since this is relevant to judge whether the effect is a general or a selective molecular mechanism since this is the one of the three assay which this comparison relies on. Alternatively, I suggest omitting this data and include the B2AR in the Live DERET assay and both B2AR and TfR in the ppH assay. Specifically, my concerns with the fixed cell internalization are: • The analysis is based on counting the number of endosomes, which is not necessarily equivalent to the number of receptors internalized

The number of puncta, as well as their fluorescence, is reported by the analysis program (written in Matlab2021 and available upon request). We chose to show number of puncta because they reflect more directly the number of labelled endosomes (in Figures 3 and 4). As shown in the figure below, we found slight but significant differences between groups for FLAG-D2R (88.6 % and 87.6 % of average fluorescence in DHA and DPA treated cells compared to control cells), (panel A), and no differences for FLAG-β2AR (panel B). We find a significant decrease in puncta fluorescence for transferrin uptake in cells incubated with DHA (but not DPA) relative to control cells (panel C). However, because we did not detect differences in the number of puncta or in the frequency and amplitude of endocytic vesicle creation events (see below), we still conclude that enrichment with exogenous PUFAs does not affect clathrin mediated endocytosis.

In conclusion, the most robust measure of endocytosis for this assay is the number of detected puncta per cell rather than their fluorescence.

• The analysis relies on fully effective stripping of the surface pool of receptors - i.e clustered surface receptors not stripped by the protocol will be assessed as internalized. It is often very difficult to obtain full efficiency of the Flag-tag stripping and this is somewhat expression dependent. • The protocol for the constitutive and agonist induced internalization is different and yet shown on the same absolute graph. Although I take it the microscope gain setting are unaltered between the constitutive and agonist induced internalization I don't believe the quantification can be directly related. This is confusing at the very least. More critically however, the membrane signal from the non-stripped condition of constitutive internalization will likely fully shield internalized receptors in the Rab4 membrane proximal recycling pathway leading to under-estimation of the in the constitutive endocytosis. I believe this methodological limitation underlies the massive relative difference in the constitutive endocytosis between panel 2A,B and 2C,D. For comparison, by a quantitative dual color FACS endocytosis assay, we have previously demonstrated the ligand endocytosis a ~4 fold increased over constitutive (in concert with Fig 2A,B here) (Schmidt et al 20XX). Importantly, high relative variability by this methodology could well shield an actual effect of incorporation of FFAs on the constitutive endocytosis. We thank the reviewer for pointing this difference in the protocol. As a matter of fact, we have not used acid stripping in all the conditions used for the uptake assays (Figures 3 and 4). We apologize for the confusion and we have clarified this point in the Methods section. In early experiments we compared conditions with or without stripping but we concluded from these experiments that indeed, the stripping was not complete. Moreover, we noticed early on that many cells treated with DHA or DPA did not have any detectable cluster (13 cells out of 58 quantified cells treated with DHA after addition of QPL, 12/56 cells treated with DPA, 0/68 for cells treated with vehicle). Stripping the antibody would have made these cells undetectable, biasing the analysis. Therefore, to make our results more consistent we decided to use non-stripping conditions. To detect endosomes specifically, we used a segmentation tool developed earlier (see Rosendale et al.* 2019). This tool is based on wavelet transforms which recognizes dot-like structures. In addition, we excluded from the cell mask the labelled plasma membrane by a mask erosion.

We agree the design of experiments was not aimed at comparing the effect of PUFA treatment on low levels of constitutive D2R endocytosis. This would require more sensitive assays and be addressed in subsequent studies.

'Optional' Also, it would be informative to see the ppH Beta-arrestin experiments with the B2AR to assess, whether the putative discrepancy between D2R and B2AR is upstream or downstream of the blunted Beta-arrestin recruitment. To the same point, it would be very informative to assess how the incorporation of the free fatty acids affect receptor signalling, which would also help relate the effect of incorporation of the FFA's in the phospholipids to previous experiment using short term incubation with FFA's

We have now performed live imaging experiments in HEK293 cells expressing SEP-β2AR, GRK2 and βarr2-mCherry and stimulated with isoproterenol (Figure EV6). We show that the clustering of SEP-β2AR, of βarr2-mCherry, as well as endocytosis, are not affected by treatments with DHA or DPA. In this study, we focused on the early trafficking steps of D2R internalization. It will be interesting in a future study to address its consequences on G protein dependent and independent signaling. Moreover, and for good measure, we performed experiments to assess TfR-SEP endocytosis with the ppH assay. Again, we found no difference between cells treated or not with PUFAs (Figure EV5)

*References overall seem appropriate although Schmidt et al would be relevant for reference of the constitutive vs agonist induced endocytosis of D2R and B2AR. *

We have now cited Schmidt et al. 2020 doi 10.1111/bcpt.13274 in the discussion with the following sentences: "D2R also shows constitutive endocytosis (Schmidt et al, 2020) which may be modulated by PUFAs although we did not detect any significant difference in our measures (see Figure 3) which were aimed at detecting high levels of internalization induced by agonists. Further work will be required to specifically examine the effect of PUFAs on constitutive GPCR internalization."

Overall, the figures are well composed and convey the messages fairly well. Specific point that would strengthen the rigor include: • Chosing actual representative pictures of the quantitative data in Fig 2 and 3 (e.g. hard to see 25 endocytic events in Fig 2A constitutive endo, EtOH)

We apologize for the confusion. We employ a normalization procedure to account for cell size. In addition, all numbers have been normalized to the condition stimulated with agonist with no PUFA treatment). In fact, we detect in unstimulated cells very few puncta (on average 0.6, range 0-5) compared to 27.3 clusters (range 2-87) in cells stimulated with QPL.

• Showing actual p values for the statistical comparisons* For easier reading, we have kept the stars convention for the figures but added two tables with all statistical tests and the p values for both main figures and EV figures.

Moreover, for ease of reading the figures (without consulting the legend repeatedly) it would be very helpful to headline individual panel with what the experiments assesses. Figure 1a and 1b for example can't be distinguished at all before reading the figure legend. Also, y-axis could be more informative on what I measured rather than just giving the unit.

We have added titles to panels (in particular for Figure 2A,B which correspond to former Figure 1A,B) and we have given new titles to Y axes to make them clearer. We hope that the reading of our figures will now be easier.

Finally, the figure presentation and description of S1 is very hard to follow. I cannot really make out what is assessed in the different panels.

We have changed substantially Figure EV1 (now Figure 1) with new presentation of data: all 4 conditions (control, treated with DHA, DPA or BA) systematically presented in the same graph, and clearer titles for the parameter displayed on the Y axes. We hope that this figure is now easier to follow.

Significance

*The strength of the manuscript is the use and validation of incorporation of FFA's in the plasma membrane, which more closely mimics the physiological situation than brief application of FFAs as often done. Is addition, the blunted recruitment of beta-arrestin as assessed by the ppH protocol is quite intriguing mechanistically. The limitation are the relative narrow focus on the D2 receptor (and not multiple GPCRs) that does not really speak to as or assess the physiological, pathophysiological or therapeutic role of the observations (except from referring the relation between FFAs and disease). Also, despite the putative role of Beta-arrestin recruitment in the process, the actual causation in the process is not clear. This shortcoming is underscored by the putative effect on the constitutive internalization described above.

My specific expertise for assessing the paper is within general trafficking processes (including the trafficking methodology applied), trafficking of GPCRs and function of the dopamine system including the role of D2 receptors.*

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

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The only conclusion that I was able to understand from the study was that enrichment of cell membranes with polyunsaturated fatty acids specifically inhibited agonist-induced internalization of D2 receptors. However, I think that the experiments used to conclude that PUFAs do not alter D2R clustering but reduce the recruitment of β-arrestin2 and D2R endocytosis need some clarification (i.e. data depicted in Fig. 2-5). This lack of clarity might be due to the fact I am not familiar enough with the employed technologies or to the unclear writing style of the paper. There was an overuse of acronyms, initialisms and abbreviations, which are difficult to understand for researchers outside of the specific lipid field. I think that the manuscript should be written in a way to be legible also for researchers not working in the immediate filed.

The paper was not written in a manner that a general audience of cell biologists or those interested in GPCR biology could understand and judge. It is indeed interesting that polyunsaturated fatty acids specifically inhibit D2R internalization in HEK293 cells, and it could be significant. But, it is difficult to judge the significance of the observation without more in vivo data.

I would suggest the following. Remove all acronyms and abbreviations. Significantly, expand the Materials and Methods section, either in the manuscript or in the Supplemental section. I suggest clearly explaining each construct used, and the function of each module in the construct, with diagrams. In addition, provide a comprehensive step by step description of each experimental protocol, providing the reader with the rationale for each step in the protocol with explanatory diagrams. The authors should also more clearly explain the rationale and logic that was utilized to make the conclusions that they did from the depicted observations. Only then can a broader audience determine if the authors' conclusions are justified.

We thank the reviewer for his/her comments. Indeed, our main message was that two types of PUFAs (DHA and DPA) specifically alter D2R endocytosis by reducing the recruitment of β-arrestin2 without changing D2R clustering at the plasma membrane. We are sorry that our writing was not clear enough. We also found out that in the last steps of the submission to Review Commons, the first paragraph of the Discussion was inadvertently erased. This made our main conclusions, summarized in this first paragraph, less clear. We have now put back this important paragraph. Moreover, we have extensively rewritten the manuscript thriving to make it as clear as possible to a large audience. We have reduced the use of acronyms to keep only the most used ones [e.g. PUFA (used 99 times), DHA (37 times), GPCR (34 times), D2R (126 times), GRK (17 times)] and made them consistent throughout the manuscript. Following the reviewer's suggestion, we have also added a scheme of the steps following D2R activation by agonist leading to its internalization (Figure EV3).

We understand that the reviewer implies by "in vivo data" results obtained in the brain of animals. As written in the Introduction and in the Discussion, the current work follows up on a recently published manuscripts by a subset of the authors, namely (i) Ducrocq et al. 2020 (doi 10.1016/j.cmet.2020.02.012) in which we show that deficits in motivation in animals deprived in ω3-PUFAs can be restored specifically by conditional expression of a fatty acid desaturase from c. elegans (FAT1) that allows restoring PUFA levels specifically in D2R-expressing striatal projection neurons (which mediate the so-called indirect pathway), and (ii) Jobin et al. 2023 (doi: 10.1038/s41380-022-01928-6) which combines in cellulo (HEK 293 cells) and in vivo data to show that PUFAs affects the ligand binding of the dopamine D2 receptor and its signaling in a lipid context that reflects patient lipid profiles regarding poly-unsaturation levels.

Reviewer #2 (Significance (Required)):

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In summary, I will reiterate that the reported experiments need to be much better explained to make the study understandable to a broader audience and for that audience to determine whether the conclusions are justified.

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

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Summary:

The authors investigate the role of lipid polyunsaturation in endocytic uptake of the dopamine D2 receptor (D2R). To modulate the degree of unsaturation in live cell plasma membranes, the authors incubate cell lines with pure fatty acid that is metabolized and incorporated into the cellular membranes. To quantify the internalization of D2R in these live cells, the authors utilized quantitative fluorescence assays such as DERET and endosome analysis to determine the degree and rate of D2R internalization in the presence of two model agonists - dopamine and quinpirole. The authors conclude that when the PUFA content of the plasma membrane is increased (i.e., via ω3 or ω6 fatty acids), both the quantity and rate of D2R internalization decrease substantially. The authors confirmed that these phenomena are specific to D2R as caveolar endocytosis and clathrin-mediated endocytosis were unaffected when these same experimental techniques were utilized for β2 adrenergic receptor and transferrin. Additionally, the authors conclude that the clustering ability of D2R is unaffected by lipid unsaturation but that the ability of D2R clusters to interact with β-arrestin2 is inhibited in the presence of excess PUFA. Based on these findings, the authors propose several hypothetical mechanisms for lipid-D2R interactions on the plasma membrane, which will likely be the scope of future work.

Overall, this is a highly thorough and rigorous body of work that convincingly illustrates the connection between PUFA levels and D2R activity. However, I do not agree with the authors' conclusions pertaining to how their results should be interpreted in the context of fatty acid-related disorders. Additionally, this manuscript could benefit from some reorganization which would present the work more clearly. Please see the comments below.

We thank the reviewer for the positive appreciation of our work, qualified as a "thorough and rigorous body of work that convincingly illustrates the connection between PUFA levels and D2R activity". We will address the specific points raised by the reviewer with our answers below.

Comments:

1. • A recurring motivation for this study that is brought up by the authors is that dietary deficiency of ω3 fatty acids is tied to D2R dysfunction. This would indicate that PUFA reduction in the plasma membrane results in D2R dysfunction. However, the experiments emphasized in this manuscript investigate the condition where PUFA content is INCREASED in the plasma membrane and D2R function is compromised. It seems inappropriate for the authors to cite dietary deficiency of ω3 as a motivation when they experimentally test a condition that is tied to ω3 surplus.* Regarding the general comment of the reviewer, we agree that direct conclusion cannot be drawn on the etiology of psychiatric disorders by looking at the effect of membrane fatty acid levels on D2R in HEK 293 cells. Nevertheless, we mention in the Introduction the intriguing occurrence of low PUFA levels in psychiatric disorders as starting point to look at D2R as an important target for psychoactive drugs prescribed for these disorders. In the Discussion, we propose that manipulating fatty acid levels might potentiate the efficacy of D2R ligands used as treatments. We felt raising these aspects was not putting too much emphasis on psychiatric disorders. However, in accordance with the reviewer's comment, we toned down these descriptions in the revised manuscript.

The goal of increasing the levels of fatty acids at the membrane in HEK 293, the most widely used cellular system to study GPCR trafficking, was to try to emulate the levels of lipids in brain cells. Indeed, the levels of PUFAs in our culture conditions are much lower (~8 %, Figure 1B) than in brain extracts (~30 %). Therefore, the "control" condition in HEK 293 cells would correspond to PUFA deficiency while after our enrichment protocol these levels are closer to those found in brain cells. Our results could therefore be interpreted as endocytosis of D2R being augmented under membrane PUFA decrease. Importantly, increased receptor internalization often correlates with decreased signaling. Therefore, membrane PUFA enrichment in our conditions would rather potentiate D2R signaling.

• Following up on the first comment, the authors' results seem to indicate that excess ω3's are detrimental to D2R function. This result would be at odds with the conventional view that ω3's are essential and that excessive ω3 may not be harmful. The authors should rationalize their findings in the context of what is known about excess dietary ω3.*

The Reviewer is right that the conventional view is that excessive ω3 PUFA may not be harmful. However, this rather applies to dietary consumption, which might have limited effect to brain fatty acid contents since their accretion is highly regulated. Moreover, the majority of studies looking at ω3 supplementation have been performed in young adults and the effects on the developing brain - as it might be happening in pathological conditions in which D2R is involved - remain poorly understood. Furthermore, as mentioned above, blunted internalization of D2R under membrane PUFA enrichment is not an indication of "detrimental" to D2R function. Nor do we argue that membrane enrichment corresponds to excess PUFAs.

• I would argue that the control experiments with saturated fatty acids (i.e., Behenic Acid in figure 1), represent a scenario mimicking ω3 deficiency as the enrichment of Behenic Acid causes an overall reduction in PUFAs (Figure EV1C - an increase in SFA must correspond to a decrease in PUFA). These Behenic acid results are the only experiments presented by the authors that mimic a scenario resembling ω3 deficiency and the results show that the D2R internalization is unaffected (Figure 1G-H). Therefore, I would further argue that if anything, the authors results suggest that ω3 deficiency is NOT correlated to D2R internalization. Again, the authors must rationalize these findings in the context of what is known about dietary intake of ω3's.*

The Reviewer must refer to the fact that nutrients rich in SFAs are usually poor in PUFAs and vice-versa. Based on our lipidomic analysis, we now present in Figure 1B the effect of treatments (DHA, DPA, BA) on the levels of PUFAs (Figure 1B) and saturated fatty acids (Figure 1C). In cells treated with behenic acid (BA), PUFA levels are not significantly changed relative to control, untreated cells, while saturated fatty acid levels are increased. BA was used here to determine whether the effects observed with PUFAs was related to the enrichment in unsaturations or due to carbon chain length (C22). It is not the case because BA treatment, unlike DHA or DPA treatment, does not affect D2R endocytosis (Figure 2G,H).

• It's not clear why the authors decided to include an ω6 fatty acid in this study. The authors built up a detailed rationale for investigating ω3's as they are dietarily essential and tied to disease when deficient. To my knowledge, ω6's are considered much less beneficial than ω3's in a dietary sense. The inclusion of an ω6 almost seems coerced as the ω6-related results don't provide any interesting additional insights. It would benefit the manuscript if the authors provided some additional discussion explaining why ω6's are being investigated in addition to ω3's. *

We agree that we could have made the rationale clearer. The goal in comparing ω3-DHA and ω6-DPA was to assess whether the position of the first unsaturation (n-3 vs n-6), with the same carbon chain length (C22) might differentially impact D2R endocytosis.

• In Figure EV1D, the AHA and DPA percentages each increase by ~6%. The corresponding Figure EV1B indicates that the overall PUFA% in the plasma membrane also increases by 6%. This makes sense as the total change in PUFA content is consistent with the amount of AHA or DPA being internalized to cells. However, this consistency was not observed with BA and SFAs. In Figure EV1E, the BA percentage increases only ~1% while the total SFA percentage in Figure EV1C increases by ~6%. How can something undergoing a 1% change (relative to total lipid content) result in a 6% overall change in SFA content?*

The reviewer is correct: the level of SFAs is increased by 5.2% (34.5 % of total FAs in control cells to 39.7 % in BA treated cells), more than the increase in BA alone (1.18% from 0.35 % to 1.53 %). A close look at our lipidomics data showed that many of the 10 saturated fatty acids quantified are enhanced. In particular, the two most abundant ones, palmitic acid (16:0) and stearic acid (18:0) are increased, from 21.37 % to 22.28 % and 8.47 % to 11.17%, respectively. The reasons for these apparent discrepancies may involve lipid metabolic pathways which convert the rare and long BA into more common and shorter SFAs to preserve lipid contents and thus membrane properties.

• In Figure 4, the discussion of kinetics does not make sense. How exactly are kinetics being monitored in this figure? (Recruitment kinetics are discussed in panels D and G)*

We wanted to convey the impression that the time to reach the peak βarr2-mCherry recruitment was shorter in PUFA-treated cells than in control cells. However, after analyzing the kinetics in individual cells, we did not find a statistically significant difference in the time to maximum fluorescence. Therefore, we removed this reference to the kinetics of recruitment.

We now write: " However, treatment with DHA or DPA significantly decreased peak βarr2-mCherry fluorescence (Figure 5F-G).."

• In Figure 5, What is the purpose of panel D? Would it be more helpful to include additional, overlaid "cumulative N" plots for scenarios in which PUFAs were enriched? This would work well in conjunction with panel F.*

The purpose of this panel is to show the kinetics of increase in the frequency of endocytic vesicle formation upon agonist addition, and the decrease in frequency when the agonist is removed. We have now added examples of cells treated with DHA and DPA of similar surface for direct comparison with control (EtOH) cells.

• For the readers who are new to this area or unfamiliar with the assays used, Figure 1 is not intuitive and initially difficult to interpret. It would greatly benefit the flow of the manuscript if Figures EV1A-C and EV2A were included in the main text and "Normalized R" was clearly defined in the main text, prior to discussion of Figure 1.*

We have now transferred Figure EV1 as Figure 1. We have adapted the scheme of the DERET assay and its legend (now in Figure EV1A) to make it clearer. We did not put in Figure 2 because this figure is already very big. We have changed "Normalized R" to "Ratio 620/520) (% max)" to be clearer and more consistent with the scheme.

Reviewer #3 (Significance (Required)):

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General assessment: The work, for the most part, is rigorous and scientifically sound. The authors utilize impressive, quantitative assays to expand our understanding of protein-lipid interactions. However, the authors need to improve their discussion of the actual physiological conditions that correspond to their experimental results.

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Advance: This work may fill a gap in our understanding of disorders related to the dopamine D2 receptor. However, some of the results may be at odds with what is currently known/understood about dietary ω3 fatty acids.

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Audience: This work will be of broad interest to researchers in the biophysics field, with particular emphasis on researchers who study protein and membrane biophysics. This work will also be of interest to researchers who study membrane molecular biology.

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Reviewer Expertise: quantitative fluorescence spectroscopy and microscopy; membrane biophysics; protein-lipid interactions

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors investigate the role of lipid polyunsaturation in endocytic uptake of the dopamine D2 receptor (D2R). To modulate the degree of unsaturation in live cell plasma membranes, the authors incubate cell lines with pure fatty acid that is metabolized and incorporated into the cellular membranes. To quantify the internalization of D2R in these live cells, the authors utilized quantitative fluorescence assays such as DERET and endosome analysis to determine the degree and rate of D2R internalization in the presence of two model agonists - dopamine and quinpirole. The authors conclude that when the PUFA content of the plasma membrane is increased (i.e., via ω3 or ω6 fatty acids), both the quantity and rate of D2R internalization decrease substantially. The authors confirmed that these phenomena are specific to D2R as caveolar endocytosis and clathrin-mediated endocytosis were unaffected when these same experimental techniques were utilized for β2 adrenergic receptor and transferrin. Additionally, the authors conclude that the clustering ability of D2R is unaffected by lipid unsaturation but that the ability of D2R clusters to interact with β-arrestin2 is inhibited in the presence of excess PUFA. Based on these findings, the authors propose several hypothetical mechanisms for lipid-D2R interactions on the plasma membrane, which will likely be the scope of future work.

Overall, this is a highly thorough and rigorous body of work that convincingly illustrates the connection between PUFA levels and D2R activity. However, I do not agree with the authors' conclusions pertaining to how their results should be interpreted in the context of fatty acid-related disorders. Additionally, this manuscript could benefit from some reorganization which would present the work more clearly. Please see the comments below.

Comments:

1. A recurring motivation for this study that is brought up by the authors is that dietary deficiency of ω3 fatty acids is tied to D2R dysfunction. This would indicate that PUFA reduction in the plasma membrane results in D2R dysfunction. However, the experiments emphasized in this manuscript investigate the condition where PUFA content is INCREASED in the plasma membrane and D2R function is compromised. It seems inappropriate for the authors to cite dietary deficiency of ω3 as a motivation when they experimentally test a condition that is tied to ω3 surplus.
2. Following up on the first comment, the authors' results seem to indicate that excess ω3's are detrimental to D2R function. This result would be at odds with the conventional view that ω3's are essential and that excessive ω3 may not be harmful. The authors should rationalize their findings in the context of what is known about excess dietary ω3.
3. I would argue that the control experiments with saturated fatty acids (i.e., Behenic Acid in figure 1), represent a scenario mimicking ω3 deficiency as the enrichment of Behenic Acid causes an overall reduction in PUFAs (Figure EV1C - an increase in SFA must correspond to a decrease in PUFA). These Behenic acid results are the only experiments presented by the authors that mimic a scenario resembling ω3 deficiency and the results show that the D2R internalization is unaffected (Figure 1G-H). Therefore, I would further argue that if anything, the authors results suggest that ω3 deficiency is NOT correlated to D2R internalization. Again, the authors must rationalize these findings in the context of what is known about dietary intake of ω3's.
4. It's not clear why the authors decided to include an ω6 fatty acid in this study. The authors built up a detailed rationale for investigating ω3's as they are dietarily essential and tied to disease when deficient. To my knowledge, ω6's are considered much less beneficial than ω3's in a dietary sense. The inclusion of an ω6 almost seems coerced as the ω6-related results don't provide any interesting additional insights. It would benefit the manuscript if the authors provided some additional discussion explaining why ω6's are being investigated in addition to ω3's.
5. In Figure EV1D, the AHA and DPA percentages each increase by ~6%. The corresponding Figure EV1B indicates that the overall PUFA% in the plasma membrane also increases by 6%. This makes sense as the total change in PUFA content is consistent with the amount of AHA or DPA being internalized to cells. However, this consistency was not observed with BA and SFAs. In Figure EV1E, the BA percentage increases only ~1% while the total SFA percentage in Figure EV1C increases by ~6%. How can something undergoing a 1% change (relative to total lipid content) result in a 6% overall change in SFA content?
6. In Figure 4, the discussion of kinetics does not make sense. How exactly are kinetics being monitored in this figure? (Recruitment kinetics are discussed in panels D and G)
7. In Figure 5, What is the purpose of panel D? Would it be more helpful to include additional, overlaid "cumulative N" plots for scenarios in which PUFAs were enriched? This would work well in conjunction with panel F.
8. For the readers who are new to this area or unfamiliar with the assays used, Figure 1 is not intuitive and initially difficult to interpret. It would greatly benefit the flow of the manuscript if Figures EV1A-C and EV2A were included in the main text and "Normalized R" was clearly defined in the main text, prior to discussion of Figure 1.

Significance

General assessment: The work, for the most part, is rigorous and scientifically sound. The authors utilize impressive, quantitative assays to expand our understanding of protein-lipid interactions. However, the authors need to improve their discussion of the actual physiological conditions that correspond to their experimental results.

Advance: This work may fill a gap in our understanding of disorders related to the dopamine D2 receptor. However, some of the results may be at odds with what is currently known/understood about dietary ω3 fatty acids.

Audience: This work will be of broad interest to researchers in the biophysics field, with particular emphasis on researchers who study protein and membrane biophysics. This work will also be of interest to researchers who study membrane molecular biology.

Reviewer Expertise: quantitative fluorescence spectroscopy and microscopy; membrane biophysics; protein-lipid interactions

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Referee #2

Evidence, reproducibility and clarity

The only conclusion that I was able to understand from the study was that enrichment of cell membranes with polyunsaturated fatty acids specifically inhibited agonist-induced internalization of D2 receptors. However, I think that the experiments used to conclude that PUFAs do not alter D2R clustering but reduce the recruitment of β-arrestin2 and D2R endocytosis need some clarification (i.e. data depicted in Fig. 2-5). This lack of clarity might be due to the fact I am not familiar enough with the employed technologies or to the unclear writing style of the paper . There was an overuse of acronyms, initialisms and abbreviations, which are difficult to understand for researchers outside of the specific lipid field. I think that the manuscript should be written in a way to be legible also for researchers not working in the immediate filed.

The paper was not written in a manner that a general audience of cell biologists or those interested in GPCR biology could understand and judge. It is indeed interesting that polyunsaturated fatty acids specifically inhibit D2R internalization in HEK293 cells, and it could be significant. But, it is difficult to judge the significance of the observation without more in vivo data.

I would suggest the following. Remove all acronyms and abbreviations. Significantly, expand the Materials and Methods section, either in the manuscript or in the Supplemental section. I suggest clearly explaining each construct used, and the function of each module in the construct, with diagrams. In addition, provide a comprehensive step by step description of each experimental protocol, providing the reader with the rationale for each step in the protocol with explanatory diagrams. The authors should also more clearly explain the rationale and logic that was utilized to make the conclusions that they did from the depicted observations. Only then can a broader audience determine if the authors' conclusions are justified.

Significance

In summary, I will reiterate that the reported experiments need to be much better explained to make the study understandable to a broader audience and for that audience to determine whether the conclusions are justified.

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Referee #1

Evidence, reproducibility and clarity

The manuscript, using different live and fixed cell trafficking assays, demonstrates that incorporation of poly-unsaturated, but not saturated, free fatty acids in the membrane phospholipids reduce agonist induced internalization of the D2 dopamine receptor but not the adrenergic beta2 receptors or the transferrin receptor. Pulsed pH (ppH) live microscopy further demonstrated that the reduced internalization by incorporation of free fatty acid was accompanied by a blunted recruitment of Beta-arrestin for the D2R.

I believe said claims put forward in the manuscript are overall well supported by the data and as such I do not believe that further experiments are necessarily needed to uphold these key claims. Also, the methodology is satisfactorily reported, and statistics are robust, although two-way Anova like used in Fig 1 seems appropriate for Fig 2 and 3

That said, I suggest that the fixed cell internalization experiments (Fig 2 and 3), which relate the effect on the D2R to B2AR and transferrin are revised. This is important since this is relevant to judge whether the effect is a general or a selective molecular mechanism since this is the one of the three assay which this comparison relies on. Alternatively, I suggest omitting this data and include the B2AR in the Live DERET assay and both B2AR and TfR in the ppH assay. Specifically, my concerns with the fixed cell internalization are:

• The analysis is based on counting the number of endosomes, which is not necessarily equivalent to the number of receptors internalized
• The analysis relies on fully effective stripping of the surface pool of receptors - i.e clustered surface receptors not stripped by the protocol will be assessed as internalized. It is often very difficult to obtain full efficiency of the Flag-tag stripping and this is somewhat expression dependent.
• The protocol for the constitutive and agonist induced internalization is different and yet shown on the same absolute graph. Although I take it the microscope gain setting are unaltered between the constitutive and agonist induced internalization I don't believe the quantification can be directly related. This is confusing at the very least. More critically however, the membrane signal from the non-stripped condition of constitutive internalization will likely fully shield internalized receptors in the Rab4 membrane proximal recycling pathway leading to under-estimation of the in the constitutive endocytosis. I believe this methodological limitation underlies the massive relative difference in the constitutive endocytosis between panel 2A,B and 2C,D. For comparison, by a quantitative dual color FACS endocytosis assay, we have previously demonstrated the ligand endocytosis a ~4 fold increased over constitutive (in concert with Fig 2A,B here) (Schmidt et al 20XX). Importantly, high relative variability by this methodology could well shield an actual effect of incorporation of FFAs on the constitutive endocytosis.

'Optional' Also, it would be informative to see the ppH Beta-arrestin experiments with the B2AR to assess, whether the putative discrepancy between D2R and B2AR is upstream or downstream of the blunted Beta-arrestin recruitment. To the same point, it would be very informative to assess how the incorporation of the free fatty acids affect receptor signalling, which would also help relate the effect of incorporation of the FFA's in the phospholipids to previous experiment using short term incubation with FFA's

References overall seem appropriate although Schmidt et al would be relevant for reference of the constitutive vs agonist induced endocytosis of D2R and B2AR. Overall, the figures are well composed and convey the messages fairly well. Specific point that would strengthen the rigor include:

• Chosing actual representative pictures of the qunatiative data in Fig 2 and 3 (e.g. har to see 25 endocytic events in Fig 2A constitutive endo, EtOH)
• Showing actual p values for the statistical comparisions

Moreover, for ease of reading the figures (without consulting the legend repeatedly) it would be very helpful to headline individual panel with what the experiments assesses. Figure 1a and 1b for example can't be distinguished at all before reading the figure legend. Also, y-axis could be more informative on what I measured rather than just giving the unit.

Finally, the figure presentation and description of S1 is very hard to follow. I cannot really make out what is assessed in the different panels.

Significance

The strength of the manuscript is the use and validation of incorporation of FFA's in the plasma membrane, which more closely mimics the physiological situation than brief application of FFAs as often done. Is addition, the blunted recruitment of beta-arrestin as assessed by the ppH protocol is quite intriguing mechanistically. The limitation are the relative narrow focus on the D2 receptor (and not multiple GPCRs) that does not really speak to as or assess the physiological, pathophysiological or therapeutic role of the observations (except from referring the relation between FFAs and disease). Also, despite the putative role of Beta-arrestin recruitment in the process, the actual causation in the process is not clear. This shortcoming is underscored by the putative effect on the constitutive internalization described above.

My specific expertise for assessing the paper is within general trafficking processes (including the trafficking methodology applied), trafficking of GPCRs and function of the dopamine system including the role of D2 receptors.

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Reply to the reviewers

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

Summary: In this paper, Dresselhaus et al (2023) investigate the possibility that known cargoes of extracellular vesicles (EVs) released at the Drosophila neuromuscular junction have cell-autonomous functions rather than functions specifically conferred as a condition of their release in EVs, in vivo. To do so, authors focus their studies on use of Tsg101-KD, a mutant of the ESCRT-I machinery, of the ESCRT EV biogenesis pathway, and are able to show that for some endogenously-expressed, fluorescently-tagged cargoes, fluorescence intensity in the pre-synaptic compartment is significantly elevated (Syt4 and Evi) and the postsynaptic intensity in the muscle is significantly decreased (Syt4, Evi, APP, and Nrg).

We note that throughout our study, we detected endogenous Nrg with a well-characterized monoclonal antibody, not a fluorescent tag. We and others previously demonstrated that endogenous Nrg detected by this antibody is trafficked from neurons into EVs, using the same pathways as other EV cargoes such as Syt4, APP and Evi (Blanchette et al., 2022; Enneking et al., 2013; Walsh et al., 2021). Thus, the EV trafficking phenotypes in our study are consistent across fluorescently tagged cargo (endogenous knockin for Syt4 and GAL4/UAS-driven for APP and Evi), as well as for untagged, endogenous Nrg, thus controlling for effects of either overexpression or tagging.

These findings suggest that these cargoes become trapped in the endosomal system (colocalizing with early, late, and recycling endosomal compartments), rather than undergoing secretion in EVs targeting post-synaptic muscle and glia as usual. This phenotype is recapitulated for select cargoes using mutants of both early and late components of ESCRT pathway machinery. They further characterize the Tsg101 mutant, demonstrating co-occurrence of an autophagic flux defect, but as the cargo phenotype is present without induction of the autophagic flux defect for their Hrs mutants, authors suggest the overlapping role of Tsg101 in autophagy is independent of its role in the ESCRT pathway/ EV secretion. Subsequently, they use previously defined functional phenotypes of the Evi (number of active zones, number of boutons, number of developmentally-arrested ghost boutons) and Syt-4 (number of transient ghost boutons and mEJPs) cargoes to show a minimal dependence on cargo delivery via ESCRT-derived EVs for these cargoes to carry out their synaptic growth and plasticity functions in vivo. However, it should be notes that for Evi/ Wg cargo, there is a slight increase in developmentally-arrested ghost boutons suggesting the cargo may not be entirely independent of EV-mediated cargo delivery. Finally, authors express an anti-GFP proteasome-directed nanobody using motor neuron or muscle-specific drivers and find that Syt4-GFP cargo doesn't enter muscle cytoplasm as fluorescence is maintained and cargo is not degraded by the muscle proteasome. While authors suggest this as evidence of EV-mediated transfer for cargo proteostasis, it is not explicitly shown that Syt4 cargo is, in fact, trafficked and degraded by the lysosome or hypothesized how Syt4 function or post-synaptic localization may be carried out independently of EVs.

We have added new data showing that Syt4 is taken up by glial and muscle phagocytosis (Fig. 7), and included in the discussion several possible interpretations for how Syt4 activity is carried out independently of its traffic into EVs. Indeed we believe it is more likely to function in the presynaptic neuron rather than the postsynaptic muscle.

Major comments:

R1.1 It is difficult to evaluate the findings of this study without knowing the extent of ESCRT pathway impairment. Please provide data quantifying the degree of knockdown/ mutant expression for each ESCRT component (i.e., western blot)

To address the reviewer’s request to specifically measure the degree of knockdown in the RNAi lines, we tested all available reagents. Unfortunately no Drosophila Tsg101 antibody exists and we did not receive a reply to our requests for a Shrub antibody. An Hrs antibody exists, but we found that none of three available Hrs RNAi lines depleted Hrs signal, or caused a phenotype similar to the HrsD28 point mutant, suggesting that they are not effective at knocking down the protein. Therefore, we were unable to specifically measure the level of depletion in motor neurons for RNAi of Tsg101, Shrub, or Hrs.

However, we can make a strong argument that our knockdowns were sufficiently effective to answer the questions in our study. We used RNAi as only one of several complementary tools to manipulate ESCRT function (i.e. we also used loss-of-function mutants (HrsD28/Deficiency) and dominant negative mutants (Vps4DN)). These mutants caused a comparable and severe loss of EVs to RNAi (Fig 2): therefore the extent of depletion in the RNAi experiments was sufficient to cause a similarly severe phenotype as genomic or DN mutations, meeting the definition of a bona fide loss-of-function. We also know, since we used these complementary strategies, that the phenotypes we observe are very unlikely to be due to off-target effects of the RNAi.

More importantly, what is directly relevant for our subsequent functional experiments is to know the extent of EV depletion, which we have explicitly measured throughout the paper. It is unclear what additional insights would be gained by knowing whether the strong Tsg101 and Shrub RNAi phenotypes are due to incomplete versus complete knockdown, given that we do measure the extent of EV depletion under these conditions. Further, we note that tsg101 null mutants die as first instar larvae (Moberg et al., 2005), raising the possibility that a more complete knockdown in neurons would be lethal early in development and make our study impossible. Indeed HrsD28 is an early stop that preserves the VHS and FYVE domains but truncates the C-terminal ⅔ of the protein. Its (occasional) survival to third instar indicates that it may be a severe hypomorph rather than a null.

We have added a sentence in the text (p12 line 21-25) to clarify that we do not know the exact extent of knockdown for our RNAi experiments, but that by genetic definitions, they meet the criteria of a loss-of-function manipulation.

R1.2 Loss of ESCRT machinery likely disrupts the release of small EVs to a significant extent; however, the authors do not show that EV release is entirely lost, only that 1) cargoes are backed up in the endosomal system due to endosomal dysfunction and 2) fluorescence of cargoes in the postsynaptic compartment is diminished. To claim that ESCRT-derived EVs with the relevant cargoes are lost, the authors should perform immunogold labelling with TEM. This would provide direct evidence that the cargoes examined here are packaged in ILVs, and that the ILVs are of a size (~50-150nm) consistent with exosomes (which should really be referred to as small extracellular vesicles (sEVs) per the minimal information for studies of extracellular vesicles (MISEV 2018 [https://doi.org/10.1080/20013078.2018.1535750]) Additionally, EM would show the loss of cargo packaging and provide information about where these cargoes localize in the presence of ESCRT mutants/loss-of-function.

EM (including some limited immunoEM) studies requested by Reviewer 1 have previously been performed in this system by us and by the Budnik and Verstreken labs (Koles et al., 2012; Korkut et al., 2009; Korkut et al., 2013; Lauwers et al., 2018; Walsh et al., 2021). MVBs at the NMJ contain ~50-100 nm ILVs, and can often be seen proximal to or fusing with the plasma membrane. Mutants such as Hsp90 that block this fusion also block EV release, arguing that these MVBs are the source of EV (Lauwers et al., 2018). By immunoEM, the EV cargo Evi localizes to MVBs (Koles et al., 2012). ~50-200 nm structures containing immunogold against Evi were also observed in the subsynaptic reticulum between the neuron and the muscle, as well as in membrane compartments in the muscle cytoplasm (Koles et al., 2012; Korkut et al., 2009). Thus, the criteria requested by the reviewer have previously been established in this system.

In response to the reviewer’s request to show that these structures are altered in ESCRT mutants, we attempted immunoEM experiments in the Tsg101KD condition. However, similar to the previously published results (Koles et al., 2012; Korkut et al., 2009), immunoEM in thick tissue such as Drosophila larval fillets is quite challenging, and we found it very difficult to retain immunogenicity together with excellent fixation and preservation of membrane structures, such that we could rigorously measure compartment morphology and size. Even if we did achieve good structural preservation, exosomes are ambiguous in complex membrane-rich tissues, since cross-sections through the extensively infolded muscle membrane (e.g. see Fig 3B) are very similar in size to EVs.

As an alternative and more robust approach, we used STED microscopy, with a resolution of ~50nm, where we could conduct a rigorous and properly powered study of directly labeled EV cargoes (New data in Fig. S1). We show that postsynaptic Nrg and APP-GFP are found in structures with a mean diameter of ~125 nm, consistent with small EVs or exosomes, and these are strongly depleted in the Tsg101KD animals (to similar levels as antibody background far from the site of EV accumulation), as expected. Note that we are able to detect particles significantly smaller than 125 nm in the distribution, suggesting that the resolution of our system is sufficient to measure EV width.

We also note that several of these cargoes are detected via an intracellular tag (Syt4, APP, Evi) or antibody against an intracellular domain (Nrg), so by topology they must be membrane-bound in the EVs rather than cleaved from the cell surface. We and others have previously shown that this postsynaptic signal is entirely derived from the presynaptic neuron, by using neuronal UAS-expression of a tagged protein, by neuronal RNAi of the endogenous gene, or by the tissue-specific tagging approach in the current manuscript (Fig. S4). We have also previously shown that these puncta contain the tetraspanin Sunglasses (CG12143/Tsp42Ej), which is an EV marker (Walsh et al., 2021). We have added new data to our manuscript (Fig. S1A) to show that neuronally-derived tetraspanin EVs are depleted in upon Tsg101KD. Therefore, the reviewer’s point “2) fluorescence of cargoes in the postsynaptic compartment is diminished.” is the most direct and sensitive test of trans-synaptic cargo transfer, and is the precise parameter that we are trying to manipulate to test the functions of this transfer.

We believe that light microscopy showing loss of presynaptically-derived cargoes in the postsynaptic region is the best and most direct argument for loss of EV secretion, compared to the ambiguity of EM. It is also exactly the method that led to the proposal for the signaling function of EVs in previous work, which our current manuscript is revisiting. We are now using improved tests of that original hypothesis by examining it in light of additional membrane trafficking mutants (and finding that it no longer holds up). Overall, given the preponderance of evidence from the preceding literature and our studies indicating that (1) these cargoes are indeed in EVs and (2) we see a strong enough depletion of transsynaptic transfer to challenge the hypothesis that EVs serve signaling functions (see R1.3 response below), we are reluctant to spend more time attempting immunoEM which is not likely to resolve membrane structures.

To address the point of EV terminology used in our manuscript, we think it is very unlikely that the postsynaptic structures are not exosomes. The criteria defined by MISEV for exosomes is that they are endosomally-derived from MVBs, ideally with the EV “caught in the act of release” upon fusion with the plasma membrane. As noted above, cargoes such as Syt4 and Evi are observed by immunoEM in MVBs, and these can be found in the process of fusing with the plasma membrane (i.e. caught in the act of release) (Koles et al., 2012; Korkut et al., 2009; Korkut et al., 2013; Lauwers et al., 2018). Mutants that block MVB fusion also block EV release at the NMJ (Lauwers et al., 2018). These EVs require ESCRT for their formation and are trapped in endosomes rather than the plasma membrane upon ESCRT depletion (this study). They depend on multiple components of the endosomal system (Rab GTPases, retromer) for their formation (Koles et al., 2012; Walsh et al., 2021). Taken together, it seems to us that there is sufficient data to argue that these are exosomes. However, as the reviewers requested, we have called them EVs in the revised paper (and only suggest they are exosomes in the discussion).

R1.3 Other biogenesis pathways utilize multivesicular bodies to generate EVs, most prominently the nSMase2/ceramide synthesis pathway (which operates in an ESCRT-independent manner). It is possible that this pathway compensates when there are defects in the canonical ESCRT pathway. Thus, it is imperative for the authors to show that the cargo secretion no longer occurs in the presence of ESCRT mutations/loss-of-function. The authors should also use nSMase2 pathway mutants to see if the phenotypes in cargo trafficking (i.e., pre/ post-synaptic protein levels) are recapitulated.

The reviewer asked us to show that cargo secretion does not occur in the ESCRT mutants. We reiterate that at the limits of detection of our assay, we see a very strong depletion of secretion__, and that EV cargo levels are not distinguishable from background (__Figure S1). Perhaps Reviewer 1’s concern is that since it would never be possible to show that we have depleted EVs completely (i.e. below the level of detection of our assays), that it is not possible to challenge the hypothesis that EV traffic is required for the proposed signaling functions of EVs. Indeed, they mention in their overall assessment “as it is unknown if minor sources of cargo+ EVs are sufficient in maintaining functional phenotype”. We do have some information on this, as described in the manuscript (p3 lines 41-43; p7 lines 25-31; p11 lines 27-30) and as follows: The critical argument against this concern is that other trafficking mutants with residual levels of EVs (rab11 or nwk) do show loss of signaling function (Blanchette et al., 2022; Korkut et al., 2013). Therefore residual EVs, even at the lower level of detection of our assay, are not enough to support signaling. The main difference is that in nwk and rab11 mutants the levels of the cargo in the donor presynaptic neuron are also strongly depleted, unlike in the ESCRT mutants. This strongly suggests that the cargoes are signaling from the presynaptic compartment, rather than in EVs. We have added the nwk mutant to show this baseline in Figure 2A,D. Similarly, our new results showing that hrs mutants retain Wg signaling while Tsg101 mutants do not, despite a similar degree of EV depletion (new data with more cargoes in Figure 2A-F), argues that residual EVs do not account for the lack of disruption of signaling. Finally, we have been transparent in our discussion that trace amounts of EVs could still exist, including by alternative pathways, but are unlikely to provide function (p11 lines 25-33).

We agree that it might be an interesting future mechanistic direction to ask if the SMase pathway works with or in parallel to the ESCRT pathway (both have been suggested in the literature). However, we do not believe that this is essential for the current work: The SMase pathway is unlikely to be “compensating”, since EVs are already very strongly depleted with ESCRT disruption alone. We also note that SMase depletion may also affect other trafficking pathways (Back et al., 2018; Choezom and Gross, 2022; Niekamp et al., 2022), and therefore might not provide any clarifying information if it did disrupt signaling. In summary, we believe the depletion we see in single ESCRT mutants is sufficient to (1) establish the role of ESCRT in EV traffic in this system, and (2) test the role of transsynaptic transfer in signaling functions of cargoes.

R1.4 The authors' findings support that cargo trafficking is affected by widespread endosomal dysfunction but doesn't cleanly prove that 1) synaptic sEV release is lost and 2) that cargo-specific sEVs are lost. As previously mentioned, loss of cargo+ ILVs in MVEs by TEM could demonstrate this, but another useful approach would be to include in vitro Drosophila primary neuronal culture/ EV isolation and mass spec/proteomic characterization studies as proof of concept. According to widely agreed upon guidelines in the EV field, the authors should directly characterize their EV population to show 1) the appropriate size distribution associated with exosomes/sEVs, 2) the presence of traditional EV markers (i.e., tetraspanins), 3) changes in overall EV count by ESCRT mutants, and 4) decreased levels of cargo(es) of interest in the presence of ESCRT mutants/loss-of-function. In vitro experiments would be particularly helpful for quantifying the degree of loss of cargo-specific EVs with each ESCRT mutant. These experiments could also investigate the possibility that cargoes are secreted in nSMase2/ Ceramide-derived EVs, by showing that EV cargo levels are unaffected in nSMase mutants.

Our data already show loss of cargo-specific EVs, defined by puncta of several independent specific cargoes in the extraneuronal space and postsynaptic muscle. To further substantiate this, we have directly characterized our EV population and shown a distribution of ~125 nm extraneuronal structures containing the transmembrane cargoes Nrg and APP (by STED) as well as Evi, Syt4 and the EV marker tetraspanin (by confocal microscopy). This addresses the (1) size distribution, (2) EV marker and (3) count criteria. All these markers (cargoes and tetraspanins) are severely depleted from the postsynaptic area in the ESCRT mutants, satisfying the (4) decreased levels criteria. As noted above, we and others have repeatedly demonstrated that these postsynaptic puncta are derived from neurons, and since we are detecting the intracellular domain in all cases, must be membrane-bound. Others have previously shown by EM that several of these markers are surrounded by membrane and derived from neuronal MVBs (see R1.2). Note that we do not believe that ESCRT mutants must necessarily cleanly show enlarged endosomes without ILVs or a class E vps compartment - instead stalled endosomes appear to be targeted for autophagy in heterogeneous intermediates (Fig 3).

We do not believe that turning to a heterologous system (e.g. cultured primary Drosophila neurons, which do not even form functional synapses) is usefully translatable to results in neurons in vivo. Data from our lab and many other systems has shown that EV biogenesis and release pathways are highly cell-type specific (p9 lines 8-12), and also differ in different regions of neurons (eg synapses vs soma) (Blanchette and Rodal, 2020). Further, keeping the experimental setup of the original for EV signaling hypothesis is a prerequisite for our improved tests of this hypothesis. We do note that APP, Evi and Syt4 have been demonstrated by us and others to be released from Drosophila S2 cells in EVs defined by differential centrifugation, sucrose gradient buoyancy, electron microscopy and mass spectrometry (Koles et al., 2012; Korkut et al., 2009; Korkut et al., 2013; Walsh et al., 2021). However even if we did measure the precise change in EV number and cargoes upon ESCRT manipulation in these heterologous cells, it would not allow us to conclude that the same quantitative change was happening in the motor neurons of interest in vivo, which is the information we need to conduct our tests of cargo signaling function. All we would learn is whether ESCRT was required in that cell type, which would not be informative for our study.

We appreciate that EV researchers working in cell culture systems often use a set of approaches including bulk isolation, EM, and mass spectrometry. Our system does not allow for these approaches, but provides complementary strengths of single EV characterization, in vivo relevance with functional assays, and a wealth of genetic tools. MISEV itself states that it does not provide a set of agreed-upon rules that can be applied generically to any experiment. We agree with the MISEV statement that we should use the best available assays for the system under investigation.

R1.5 During functional tests of Evi+ motor neurons lacking generation of Evi+ EVs, there is a slight defect observed, namely the increased formation of developmentally arrested ghost boutons when Evi secretion in sEVs is lost. As mentioned, Evi is a transporter of Wg and it is possible for Wg to be transmitted between cells via normal diffusion. Thus, some basal levels of Wg may be reaching the muscle when its transfer via sEVs is abolished, and these basal levels may be sufficient to phenocopy the WT in the number of active zones and boutons. Is it possible that this element of Evi/ Wg function is dose-dependent and thus reliant on the extra Evi/ Wg transferred via sEVs? If possible, the authors should use a Wnt-signaling pathway reporter (i.e., fluorescently tagged Beta-Catenin) to measure the levels of Wnt signaling activity in the muscle when Evi/Wg+ EVs are present vs. abolished. If the degree of Wnt signaling (readout would be intensity of fluorescent reporter) is decreased without Evi+ sEVs, there may be a dose-dependent response. Otherwise, please more clearly disclose the partial loss of Evi function without Evi+ sEVs or state the intact function of Evi without sEVs as speculative.

We agree that Wg is likely to be reaching the muscle in the absence of Evi exosomes via conventional secretory mechanisms, and have conducted new experiments to test this hypothesis (Fig. 5). In Drosophila muscles, Wg does not signal via a conventional b-catenin pathway. Instead, neuronally-derived Wg activates cleavage of its receptor Fz2, resulting in translocation of a Fz2 C-terminal fragment into the nucleus (Mathew et al., 2005; Mosca and Schwarz, 2010). We did attempt to directly measure Wg (using antibodies or knockins) and though we were able to detect a specific presynaptic signal, the background noise throughout the postsynaptic muscle was too high for a sensible quantification. In response to the reviewer’s question and also R2.6), we collaborated with the laboratory of Timothy Mosca to test Fz2 nuclear import in Tsg101 and Hrs mutants (new Figure 5F-G). Strikingly, we found that Hrs mutants, despite being extremely sickly, have normal nuclear import of Frizzled. We also confirmed that Hrs mutants have dramatically depleted levels of all EV cargoes examined, including Evi (Figure 2A-F). On the other hand we found that Tsg101 knockdowns have dramatically reduced Wg signaling (and a concomitant defect in postsynaptic development). We do not rule out (but think it is unlikely) that very small amounts of EVs could be present in hrs but not tsg101 mutants. A more parsimonious interpretation is that additional membrane trafficking defects in the Tsg101 mutants (which are beyond the scope of this study to explore in detail) block an alternative mode of Wg release, perhaps conventional secretion. The fact that Hrs mutants, despite showing similar depletion of Evi EVs, do not have a signaling defect strongly argues that EV release per se is not required for Wg signaling.

R1.6 To support the authors' hypothesis that Syt4 transmission via EVs is a proteostatic mechanism, the authors should determine whether Syt4 cargo localizes to lysosomal compartments in muscle, glia, or both. Otherwise, the proteostatic degradation of Syt4 via EVs is speculative.

Our data suggest that EVs serve as one of several parallel proteostatic mechanisms for presynaptic cargoes. We have added new data to the manuscript to emphasize the advance our work makes in our understanding of these mechanisms, and have emphasized this in the discussion on p 11-12, lines 46-5).

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1. Degradation of neuronally derived EVs in glia and muscles. Previous work has shown that EV cargoes such as Evi can be found in compartments in the muscle cytoplasm, and that a-HRP-positive puncta are taken up and degraded by glial and muscle phagocytosis (Fuentes-Medel et al., 2009). These a-HRP-positive structures, despite colocalizing with EV cargoes Syt4, Nrg and APP (Walsh et al., 2021), were not previously connected to EVs. We have added new data showing that muscle or glial-specific RNAi of the phagocytic receptor Draper leads to the accumulation of EVs containing Syt4 (new Figure 7G-H)). Together with our finding (Figure 7A-F) that Syt4 is not significantly detected in the muscle cytoplasm, these results indicate that the main destination for transynaptic transfer is phagocytosis by the recipient cell. We have not been able to convincingly detect EV cargoes in the endolysosomal system of muscles, even in mutants disrupting lysosomal traffic, likely because the small number of EVs released by neurons (even over days of development) are drastically diluted in the much larger muscle cell.
2. Compensatory endosomophagy in the neuron. __When EV release is blocked in Hrs or Tsg101 mutants, we observe an induction of autophagy in the neuron (__Figure 3B, E-G). However, in the absence of ESCRT manipulation, autophagy mutants do not accumulate EVs (Figure 3C,D. S2H-I). This suggests that autophagy is a compensatory mechanism that is induced in the absence of EV release.
3. Retrograde transport to cell bodies: We previously found that disruption of neuronal dynactin leads to accumulation EV cargoes in presynaptic terminals (Blanchette et al., 2022), suggesting that retrograde transport is a mechanism for removal of these cargoes from synapses. Interestingly, EV release is not increased in these conditions, indicating that the retrogradely transported compartment represents a late endosome without ILVs, or an MVB that cannot fuse with the plasma membrane.

   R1.7 Please discuss alternate modes of cargo transfer from the presynaptic compartment to the postsynaptic compartment that may be utilized when EV-mediated transfer is abolished (i.e., cytonemes or tunneling nanotubules).

We have added these possibilities to the discussion (p11 line 31), though we note that we do not observe any such structures, or indeed any Syt4 in the muscle cytoplasm, and there is no current evidence for such transsynaptic structures in this system. Conventional secretion of Wg into the extracellular space and signaling through its transmembrane receptor Frizzled2 can account for Wg signaling in the absence of exosomes.

R1.8 OPTIONAL: Investigate the mechanism of Syt4+ sEV fusion with the postsynaptic compartment (direct fusion with the plasma membrane, receptor-mediated fusion, endocytosis and unpacking, or endocytosis and degradation).

We note that the Budnik lab has already shown that HRP-positive EVs released by NMJs are taken up by glia and muscles (Fuentes-Medel et al., 2009), and we have added data showing that this also applies for Syt4 (Fig. 7). Our data are not consistent with Syt4 fusing with recipient cell membranes or entering the muscle cytoplasm. Further investigation of this mechanism is beyond the scope of this project.

Given that several fundamental questions have yet to be answered regarding the biogenesis pathways and machinery utilized for EV-mediated cargo secretion, and the necessity for further TEM studies and/or work with primary cultures to characterize ILVs and EVs, >6 months is estimated to perform the necessary experiments that may require learning/ optimizing new systems.

Minor comments:

R1.9 Please clarify the choice of using Tsg101 KD in place of mutants of other ESCRT machinery (i.e., Hrs). Especially as when the Tsg101 mutant was characterized, you found major defects in autophagic flux that were not present for HrsD28/Df.

Tsg101 RNAi was selected since it provides a neuron-autonomous knockdown, eliminating the complications of mutant effects in other tissues. These animals are also relatively healthy as third instar larvae compared to genomic mutants tsg1012 (L1 lethal) and HrsD28 or motor-neuron driven Vps4DN (where L3 larvae are rare). This made it easier to recover enough larvae to properly power experiments, and alleviated concerns that general sickness is contributing to the phenotype (though note that neuronal Tsg101KD does result in pupal lethality). Finally, we were unable to effectively knock down Hrs by RNAi (see R1.1). To extend our studies beyond Tsg101, we have included additional experiments in the revised manuscript showing that HrsD28 animals, despite being quite unhealthy, still retain Syt4-dependent functional plasticity (See R2.5 and R3.4) and Wg signaling.

R1.10 Please clarify why the specific method in experiment in Fig. 4E-J was chosen. As Syt4 is a transmembrane protein, is likely undergoes degradation via the lysosome, like other membrane-bound proteins. Is it known whether the proteasome-directed nanobody is sufficient to pull Syt4 from membrane-bound compartments to undergo degradation in the proteasome? Would it make more sense to use a lysosome-directed nanobody?

The GFP tag on Syt4 is cytosolic rather than lumenal. Our data show that when we express the proteosome-directed nanobody presynaptically, it efficiently degrades membrane-associated Syt4-GFP (Fig. 7B). Therefore we expect that this tool should be similarly effective on membrane-associated Syt4-GFP if it were exposed to the muscle cytoplasm. We have confirmed that it is effective in the muscle against DLG-GFP (Fig. S5A)

R1.11 Please provide further methodological information regarding the sample preparation for live imaging of axons to generate kymographs found in Fig. S3.

Additional details have been provided on p14 lines 10-24 and p15 lines 31-37.

R1.12 In Figure 1I and 1J, include representative image and quantification of Syt4-GFP pre- and post-synaptic intensity for HrsD28/Df for consistency with ShrubKD and Vps4DN in Figure 1K-P.

We generated and tested HrsD28; Syt4-GFP (Fig 2A,D), and HrsD28; Evi-GFP strains (Fig 2B-E). All EV cargoes exhibited a dramatic post-synaptic depletion in Hrs mutants, similar to the other ESCRT manipulations.

R1.13 In Figure 2H, please provide a cell type marker or HRP mask with a merged image for image clarity.

This image shows neuronal cell bodies in the ventral ganglion, which are densely packed relative to each other. The cell type specificity is provided by the motor neuron driver. We did not use a cell type marker or individually mask cells for analysis, but instead quantified intensity over the whole field of view. We can manually trace cell bodies in this image if requested, but it would not represent our ROI for analysis.

R1.14 In Figure 4B, please provide quantification for the differences between 1) WT Mock and Tsg101 MOCK and 2) WT Stim and Tsg101KD Stim to show that upon stimulation, WT and Tsg101 undergo the same increase in the number of ghost boutons/ NMJ in Muscle 4.

We have added these statistical comparisons to the graph (Fig. 6B)

R1.15 In Figure 3 G and H, use consistent scale bars to compare between temperatures.

We have removed the Shrub data at 20º as it did not provide additional insight to the manuscript.

Reviewer #1 (Significance (Required)):

General assessment (Strengths):

-Use of Drosophila NMJ model system consistent with others in the field and exceptional harnessing of genetic tools for mutations across the ESCRT pathway (-0, -I, -III, etc.) -Identification of ESCRT pathway mutants that do not deplete pre-synaptic cargo levels but generate endosomal dysfunction, indicative of a possible decrease in secretion of cargoes via EVs -Implementing functional characterization of Evi/ Wg and Syt4 cargoes, consistent with previous work in the field; highly reproducible

-Sufficiently thorough investigation of the cross-regulation of autophagy and EV biogenesis by Tsg101

General assessment (Weaknesses):

-Lack of investigation of known ESCRT-independent pathways/ genes involved in the generation of sEVs (i.e., nSMase2/ Ceramide) especially as it is unknown if minor sources of cargo+ EVs are sufficient in maintaining functional phenotype

See R1.3 for comments on this point

-Lack of sEV characterization and validation of EVs derived from mutant

We have added STED data to measure EV size, and described the challenges in EV membrane measurements by EM in the in vivo system.

-Does not show the loss of cargoes of interest on EVs from mutants other than through back-up of cargoes in the presynaptic endocytic pathway (Rab7, Rab5, Rab11)

We strongly disagree with this comment. We have explicitly measured the loss of numerous cargoes in postsynaptic structures that have been rigorously established to be EVs in this and previous publications. Our findings are not limited to back-up of presynaptic structures.

-Lack of rigorous investigation of the claim that Evi and Syt4 are released via EVs for proteostatic means is missing. Authors should demonstrate the degradation of EV cargoes by recipient cells (either muscle OR glia)

We have added new data and discussion on multiple and compensatory proteostatic pathways.

-If EV-mediated cargo transfer is not required, authors should investigate alternate modes of cargo transfer more rigorously (i.e., diffusion of Wg, suggest/ test hypotheses for mechanism of Syt4 function or transfer).

We have included discussion of alternate modes of transfer for Wg (i.e. conventional secretion). By contrast, for Syt4 we believe it is acting in the donor cell without transfer, and have included alternate interpretations of the previous literature that had suggested its function in muscles.

Advance: -Compared with other recent in vivo studies of EVs where donor EVs are loaded with a cargo, such as Cre, which uniquely identifies recipient cells through Cre recombination-mediated expression of a fluorescent reporter (Zomer et al 2015, Cell), this study relies on the readout of fluorescently tagged cargo in the recipient cells to represent transfer via EVs. While numerous studies in the Drosophila field focus on the same small set of known EV cargoes at the NMJ (Koles et al., 2012; Gross et al., 2012; Korkut et al., 2013; Korkut et al., 2009; Walsh et al., 2021), there is a noticeable lack of EV characterization based on MISEV (i.e. TEM of EVs, size distribution, enrichment of well-known EV markers [https://doi.org/10.1080/20013078.2018.1535750]) that would significantly strengthen the work and make it more widely accepted in the EV field.

As mentioned above, many of these criteria (including EV size and enrichment of known EV markers) are already established in the previous literature for this system. As requested, we have also added similar data to our revised manuscript.

-In this study, the use of ESCRT machinery mutants is proven as a new technical method in delineating the role of EV cargoes in cell-autonomous versus EV-dependent functions. This is the first study, to my knowledge, that has leveraged mutants from both early and late ESCRT complexes for the study of EVs in Drosophila. Additionally, the finding that some cargoes may be able to carry out their signaling functions, independent of transfer via EVs, provides key mechanistic insight into one possible role of EVs as proteostatic shuttles for cargo. This work also begins to address a fundamental question in the field, which is to delineate roles that EVs actually carry out in physiological conditions, compared to the many roles that have been shown possible in vitro.

We appreciate the reviewer’s insight into the impact of our work.

Audience: -Basic research (endosomal biology, ESCRT pathway, cell signaling, neurodevelopment)

-Specialized (Drosophila, Neurobiology; Extracellular Vesicles)

-This article will be of interest to basic scientists in the field of endosomal trafficking and extracellular vesicle biology as well as though studying the nervous system in Drosophila melanogaster. As the field of extracellular vesicle biology has broad implications in the spread of pathogenic cargoes in cancer and neurodegenerative disease, the basic biology associated with EVs has some translational relevance.

Expertise (Keywords):

-ESCRT and nSMase2 EV biogenesis pathways

-EV characterization in vitro/ live imaging studies

-EV release and uptake

-Neuronal and glial cell biology

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

This manuscript addresses the role of exosome secretion in neuromuscular junction development in Drosophila, a system that has been proposed to depend on exosomes. In particular, delivery of Wingless via exosomes has been proposed to promote structural organization of the synapse. Previously, however, the studies that proposed this model targeted the cargoes themselves, rather than targeting exosome biogenesis or secretion. In this new study, exosome biogenesis is targeted via knockdown of the ESCRT components Hrs, TSG101, and Chmp4. The authors find that some previously ascribed functions are not inhibited by these knockdowns. In particular, formation of active zones, as defined by BRP-positive puncta (total and per micrometer), and total bouton numbers. It does look like there is a partial defect in BRP-positive puncta per micrometer, but it is not significant. For ghost bouton formation, there is a similar increase in evi-mutant and ESCRT-KD NMJs (with some subtle differences depending on abdominal segment and temperature). They also examine the role of Syt4, which has been proposed to be transferred from nerve to muscle cells at the junction and to regulate mEJP frequency after stimulation. They found no difference in mEJP frequency after stimulation between WT and TSG101-KD animals, although they did not have a positive control with inhibition of Syt4. They did do an elegant experiment to demonstrate that most of extracellularly transferred Syt4 does not reach the muscle cytoplasm. Overall, it is an interesting paper, mostly well controlled and rigorous, and well-written. It is an important contribution to the EV and NMJ fields. The data should provoke reconsideration of some of the functions that were previously ascribed to exosome transfer at the NMJ. However, I do think that there are some overly strong statements and the functions of the exosomes at the synapse were quite narrowly examined. For example, the title of the paper is pretty strong and the abstract does not say which functions were or were not affected by TSG101 KD. There are also a couple of experiments that would enhance the manuscript. Some specific suggestions are below:

R2.1 Title: "ESCRT disruption provides evidence against signaling functions for synaptic exosomes" seems a bit broad -- only evi/Wg and Syt4 functions were examined at NMJ synapses, not all signaling functions of all exosomes at all synapses. Something like, "ESCRT disruption provides evidence against signaling functions for exosome-carried evi/Wg and Syt4 at the neuromuscular junction" seems a bit more reasonable.

We are open to changing the title to: “ESCRT disruption provides evidence against transsynaptic signaling functions for some extracellular vesicle cargoes” though we prefer to leave it as is since “provides evidence against” is already fairly understated.

__ __R2.2 Abstract: the description of the actual data is very little, just one sentence saying that "many" of the signaling functions are retained with ESCRT depletion. I think a bit more focus on the actual data is warranted.

We have edited the abstract to include more detail on the signaling phenotypes.

__

__R2.3 Results section:

Fig 3: What does A2 and A3 mean for the graphs in c,d,e, g, h? Please specify in figure legend.

We have described in the figure legends that A2 and A3 refer to specific abdominal segments in the larvae.

R2.4 The sentence "Further, active zones in Tsg101KD appeared morphologically normal by TEM (Fig.2B)." is confusing to me. What do you mean by that? Are you referring to the following two sentences about feathery DLG and SSR? But the feathery DLG I presume is in Fig 3, where that staining is. And I also don't know what feathery DLG means -- it should be pointed out in the appropriate image.

Presynaptic active zones are defined by an electron-dense T-shaped pedestal at sites of synaptic vesicle release, and can be seen in the TEM in what is now Figure 3B, marked as AZ. We have also labeled AZ by immunofluorescence (Fig. 5A) and they appear normal.

By contrast, Dlg primarily labels the postsynaptic apparatus associated with the infoldings of the muscle membrane. In control animals, Dlg immunostaining is relatively tightly and smoothly clustered within ~1µm of the presynaptic neuron. By contrast, in Evi mutants, there are wisps of Dlg-positive structures extending from the bouton periphery. We have added arrows in what is now Fig. 5C to indicate the feathery structures.

R2.5 Fig 4 addresses Syt4 function. However, there is no positive control inhibiting Syt4 to see if there is a change. Just comparison of WT and TSG101. It seems like this positive control is in order.

We have added the positive control (Fig. 6E-F) reproducing the previously reported result that Syt4 mutants lack the high-frequency stimulation-induced increase in mEPSP frequency (HFMR). We have also added new data on HrsD28 genomic mutants. Despite the fact that few of these larvae survive and they are quite unhealthy, they still exhibit robust HFMR, similar to the Tsg101KD larvae, strongly supporting our hypothesis.

R2.6 Discussion: I think some discussion of what ghost boutons are and what the possible significance is of the evi and ESCRT mutant phenotype of enhanced ghost bouton formation

We have added more discussion on the ghost bouton phenotype (p11 lines 5-14), especially in light of our new findings that Hrs and Tsg101 mutants may distinguish alternative modes of Wg secretion (see R1.5)

R2.7 Also, in the Discussion, it is mentioned that Wg probably gets secreted in the ESCRT mutants -- presumably this accounts for the discrepancy between evi mutants and the ESCRT mutants. An experiment to actually test this would greatly enhance the manuscript.

We have added this experiment as addressed in R1.5

Reviewer #2 (Significance (Required)):

Overall, it is an interesting paper, mostly well controlled and rigorous, and well-written. It is an important contribution to the EV and NMJ fields. The data should provoke reconsideration of some of the functions that were previously ascribed to exosome transfer at the NMJ. However, I do think that there are some overly strong statements and the functions of the exosomes at the synapse were quite narrowly examined. For example, the title of the paper is pretty strong and the abstract does not say which functions were or were not affected by TSG101 KD.

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

Dresselhaus et al. investigates signaling functions for synaptic exosomes at the Drosophila NMJ. Exosomes are widely seen in vivo and in vitro. They are clearly sufficient to induce signaling responses in vitro, but whether they normally fulfill signaling functions in vivo has not been rigorously addressed. The authors make use of several mutants that block exosome release to test whether exosome release is important for two distinct signaling pathways: the Evi/Wg pathway and the Syt4 signaling pathway. Both pathways have been implicated in neuron to muscle signaling. Surprisingly, the authors find scant evidence that exosome release is required for either pathway. They convincingly show that knockdown of Tsg101 (an ESCRT-I component) does not phenocopy many synaptic phenotypes of either wg or syt4. Instead, they propose that in vivo, exosomes may serve as a proteostatic mechanism, as a mechanism for the neuron to dispose of unwanted/damaged proteins.

Specific comments are below:

R3.1 Loss of Tsg101 has been linked to upregulated MAPK stress signaling pathways and autophagy. Thus, it's possible that activating such compensatory mechanisms in Tsg101 knockdown animals could mask phenotypes associated with specific loss of EV cargoes such as Wg or Syt4. Indeed, the authors demonstrate that loss of Tsg101 and Hrs have very different effects on synaptic autophagy. To provide additional evidence that Wg or Syt4 signaling is independent of EV release, it would be good to check for wg/syt4 phenocopy in additional ESCRT complex mutants. I understand they did a bit with Shrub knockdown at low temperature in Figure 3, but the temperature-dependence of the ghost bouton phenotype clouds the interpretation. Could the authors try a motorneuron driver with a more restricted phenotype to overcome the lethality issues, or alternatively use one of their other ESCRT component mutants? This is obviously the central claim of the manuscript, and it would be strengthened by carrying out phenotypic analysis in mutants other than the Tsg101 RNAi line.

As noted for R2.5, we have added HFMR experiments for the HrsD28 genomic mutant, and found that despite being very unhealthy, they exhibit robust HFMR similar to Tsg101KD. We also confirmed dramatic depletion of Syt4 EVs in the HrsD28 mutant. Thus, the preserved Syt4 signaling function in ESCRT mutants with depleted EV Syt4 is not restricted to Tsg101, and does not depend on the co-occurring autophagy phenotype.

R3.2 In Figure 1, the authors show that neuronal Tsg101 RNAi dramatically reduces "postsynaptic" levels of exosome cargoes at the L3 stage to argue that exosome release is blocked in this mutant. While this seems very likely at the L3 stage, it is unclear when Tsg101 levels are reduced and thus when exosome release is impaired in this background. This is important because we don't know when these signaling pathways act. For example, it is possible that the critical period for Wg and Syt4 signaling is during the L1 stage, and that Tsg101 knockdown is incomplete at that stage. It is important to assay exosome release at earlier larval stage, particularly when RNAi is the method used to reduce gene function.

We have conducted this experiment. We noted accumulation of cargoes in Tsg101KD L1 larvae, indicating that the RNAi is effective early in development. However, we do not find many EVs in either wild-type or Tsg101KD first instar larvae (red is a-HRP, green is Syt4-GFP). This argues that it is unlikely that EV-mediated signaling has a critical period earlier in development. It is likely that the accumulation of EVs that we observe trapped in the muscle membrane reticulum in third instar larvae were laid down over days or hours of development. We do not propose to include these data in the manuscript unless the editors and reviewers prefer that we do so.

R3.3 If the Syt4 and Evi exosomes do not serve major signaling roles and are in fact neuronal waste, it seems likely they are phagocytosed by glia. Are levels of non-neuronal Syt4/Evi levels increased when glial phagocytosis in blocked (eg in draper mutants)?

As mentioned above, the Budnik lab previously showed that uptake and degradation of postsynaptic a-HRP-positive structures depends on glial and muscle phagocytosis.a-HRP recognizes a number of neuronally-derived glycoproteins (Snow et al., 1987). Though the Budnik lab had not previously linked these structures to EVs, we do know that they very strongly colocalize with known EV cargoes and depend on the exact same membrane traffic machinery for release, arguing that some a-HRP antigen proteins are also EV cargoes (Blanchette et al., 2022). To close this loop. we have added data showing that Syt4-positive EVs also depend on Draper for their clearance (Fig 7).

R3.4 For the HFMR experiment, it would be good to see the syt4-dependent phenotype as a positive control.__ __

As mentioned for R2.5, we have added the Syt4 positive control (Figure 6E,F), which fails to show HFMR as expected.

.__ __R3.5 In the abstract, the authors state that, "the cargoes are likely to function cell autonomously in the motorneuron". Isn't it alternatively possible that these proteins (wg in particular) could signal to the muscle in a non-exosome dependent pathway?

Yes, we believe that Wg is likely released by another mechanism (perhaps conventional secretion). As noted for R1.5 and R2.6, we have added new data in Fig. 5 showing that Frizzled nuclear import IS NOT disrupted in Hrs mutants, despite dramatic loss of Evi EVs. Interestingly Frizzled nuclear import (and postsynaptic development) IS altered in neuronal Tsg101KD larvae, which disrupt additional membrane trafficking pathways beyond EV release (see Fig. 3). This is particularly interesting in light of the normal Syt4 signaling in Tsg101KD larvae, and supports the hypothesis that Syt4 can function without leaving the neuron, while Wg must be released, albeit not via Hrs-dependent EV formation. Another (less parsimonious) interpretation is that very small amounts of Wg release in the Hrs mutant are sufficient to promote Frizzled nuclear import.

Reviewer #3 (Significance (Required)):

This is an important paper that is well-organized and logically presented. It makes a clear and largely compelling case against major signaling roles for exosomes at this synapse. The authors should be commended for publishing this work, which demands a re-evaluation of proposed key roles for exosomes at the fly NMJ. Given the intense interest in exosomes in neurobiology, this paper will be of great interest to neuronal cell biologists working across systems.

We thank the reviewer for their appreciation of the impact of our work on the field.

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Referee #3

Evidence, reproducibility and clarity

Dresselhaus et al. investigates signaling functions for synaptic exosomes at the Drosophila NMJ. Exosomes are widely seen in vivo and in vitro. They are clearly sufficient to induce signaling responses in vitro, but whether they normally fulfill signaling functions in vivo has not been rigorously addressed. The authors make use of several mutants that block exosome release to test whether exosome release is important for two distinct signaling pathways: the Evi/Wg pathway and the Syt4 signaling pathway. Both pathways have been implicated in neuron to muscle signaling. Surprisingly, the authors find scant evidence that exosome release is required for either pathway. They convincingly show that knockdown of Tsg101 (an ESCRT-I component) does not phenocopy many synaptic phenotypes of either wg or syt4. Instead, they propose that in vivo, exosomes may serve as a proteostatic mechanism, as a mechanism for the neuron to dispose of unwanted/damaged proteins.

Specific comments are below:

Loss of Tsg101 has been linked to upregulated MAPK stress signaling pathways and autophagy. Thus, it's possible that activating such compensatory mechanisms in Tsg101 knockdown animals could mask phenotypes associated with specific loss of EV cargoes such as Wg or Syt4. Indeed, the authors demonstrate that loss of Tsg101 and Hrs have very different effects on synaptic autophagy. To provide additional evidence that Wg or Syt4 signaling is independent of EV release, it would be good to check for wg/syt4 phenocopy in additional ESCRT complex mutants. I understand they did a bit with Shrub knockdown at low temperature in Figure 3, but the temperature-dependence of the ghost bouton phenotype clouds the interpretation. Could the authors try a motorneuron driver with a more restricted phenotype to overcome the lethality issues, or alternatively use one of their other ESCRT component mutants? This is obviously the central claim of the manuscript, and it would be strengthened by carrying out phenotypic analysis in mutants other than the Tsg101 RNAi line.

In Figure 1, the authors show that neuronal Tsg101 RNAi dramatically reduces "postsynaptic" levels of exosome cargoes at the L3 stage to argue that exosome release is blocked in this mutant. While this seems very likely at the L3 stage, it is unclear when Tsg101 levels are reduced and thus when exosome release is impaired in this background. This is important because we don't know when these signaling pathways act. For example, it is possible that the critical period for Wg and Syt4 signaling is during the L1 stage, and that Tsg101 knockdown is incomplete at that stage. It is important to assay exosome release at earlier larval stage, particularly when RNAi is the method used to reduce gene function.

If the Syt4 and Evi exosomes do not serve major signaling roles and are in fact neuronal waste, it seems likely they are phagocytosed by glia. Are levels of non-neuronal Syt4/Evi levels increased when glial phagocytosis in blocked (eg in draper mutants)?

For the HFMR experiment, it would be good to see the syt4-dependent phenotype as a positive control.

In the abstract, the authors state that, "the cargoes are likely to function cell autonomously in the motorneuron". Isn't it alternatively possible that these proteins (wg in particular) could signal to the muscle in a non-exosome dependent pathway?

Significance

This is an important paper that is well-organized and logically presented. It makes a clear and largely compelling case against major signaling roles for exosomes at this synapse. The authors should be commended for publishing this work, which demands a re-evaluation of proposed key roles for exosomes at the fly NMJ. Given the intense interest in exosomes in neurobiology, this paper will be of great interest to neuronal cell biologists working across systems.

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

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

This manuscript addresses the role of exosome secretion in neuromuscular junction development in Drosophila, a system that has been proposed to depend on exosomes. In particular, delivery of Wingless via exosomes has been proposed to promote structural organization of the synapse. Previously, however, the studies that proposed this model targeted the cargoes themselves, rather than targeting exosome biogenesis or secretion. In this new study, exosome biogenesis is targeted via knockdown of the ESCRT components Hrs, TSG101, and Chmp4. The authors find that some previously ascribed functions are not inhibited by these knockdowns. In particular, formation of active zones, as defined by BRP-positive puncta (total and per micrometer), and total bouton numbers. It does look like there is a partial defect in BRP-positive puncta per micrometer, but it is not significant. For ghost bouton formation, there is a similar increase in evi-mutant and ESCRT-KD NMJs (with some subtle differences depending on abdominal segment and temperature). They also examine the role of Syt4, which has been proposed to be transferred from nerve to muscle cells at the junction and to regulate mEJP frequency after stimulation. They found no difference in mEJP frequency after stimulation between WT and TSG101-KD animals, although they did not have a positive control with inhibition of Syt4. They did do an elegant experiment to demonstrate that most of extracellularly transferred Syt4 does not reach the muscle cytoplasm. Overall, it is an interesting paper, mostly well controlled and rigorous, and well-written. It is an important contribution to the EV and NMJ fields. The data should provoke reconsideration of some of the functions that were previously ascribed to exosome transfer at the NMJ. However, I do think that there are some overly strong statements and the functions of the exosomes at the synapse were quite narrowly examined. For example, the title of the paper is pretty strong and the abstract does not say which functions were or were not affected by TSG101 KD. There are also a couple of experiments that would enhance the manuscript. Some specific suggestions are below:

Title: "ESCRT disruption provides evidence against signaling functions for synaptic exosomes" seems a bit broad -- only evi/Wg and Syt4 functions were examined at NMJ synapses, not all signaling functions of all exosomes at all synapses. Something like, "ESCRT disruption provides evidence against signaling functions for exosome-carried evi/Wg and Syt4 at the neuromuscular junction" seems a bit more reasonable.

Abstract: the description of the actual data is very little, just one sentence saying that "many" of the signaling functions are retained with ESCRT depletion. I think a bit more focus on the actual data is warranted.

Results section: Fig 3: What does A2 and A3 mean for the graphs in c,d,e, g, h? Please specify in figure legend.

The sentence "Further, active zones in Tsg101KD appeared morphologically normal by TEM (Fig. 2B)." is confusing to me. What do you mean by that? Are you referring to the following two sentences about feathery DLG and SSR? But the feathery DLG I presume is in Fig 3, where that staining is. And I also don't know what feathery DLG means -- it should be pointed out in the appropriate image.

Fig 4 addresses Syt4 function. However, there is no positive control inhibiting Syt4 to see if there is a change. Just comparison of WT and TSG101. It seems like this positive control is in order. Discussion: I think some discussion of what ghost boutons are and what the possible significance is of the evi and ESCRT mutant phenotype of enhanced ghost bouton formation

Also, in the Discussion, it is mentioned that Wg probably gets secreted in the ESCRT mutants -- presumably this accounts for the discrepancy between evi mutants and the ESCRT mutants. An experiment to actually test this would greatly enhance the manuscript.

Significance

Overall, it is an interesting paper, mostly well controlled and rigorous, and well-written. It is an important contribution to the EV and NMJ fields. The data should provoke reconsideration of some of the functions that were previously ascribed to exosome transfer at the NMJ. However, I do think that there are some overly strong statements and the functions of the exosomes at the synapse were quite narrowly examined. For example, the title of the paper is pretty strong and the abstract does not say which functions were or were not affected by TSG101 KD.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this paper, Dresselhaus et al (2023) investigate the possibility that known cargoes of extracellular vesicles (EVs) released at the Drosophila neuromuscular junction have cell-autonomous functions rather than functions specifically conferred as a condition of their release in EVs, in vivo. To do so, authors focus their studies on use of Tsg101-KD, a mutant of the ESCRT-I machinery, of the ESCRT EV biogenesis pathway, and are able to show that for some endogenously-expressed, fluorescently-tagged cargoes, fluorescence intensity in the pre-synaptic compartment is significantly elevated (Syt4 and Evi) and the postsynaptic intensity in the muscle is significantly decreased (Syt4, Evi, APP, and Nrg). These findings suggest that these cargoes become trapped in the endosomal system (colocalizing with early, late, and recycling endosomal compartments), rather than undergoing secretion in EVs targeting post-synaptic muscle and glia as usual. This phenotype is recapitulated for select cargoes using mutants of both early and late components of ESCRT pathway machinery. They further characterize the Tsg101 mutant, demonstrating co-occurrence of an autophagic flux defect , but as the cargo phenotype is present without induction of the autophagic flux defect for their Hrs mutants, authors suggest the overlapping role of Tsg101 in autophagy is independent of its role in the ESCRT pathway/ EV secretion. Subsequently, they use previously defined functional phenotypes of the Evi (number of active zones, number of boutons, number of developmentally-arrested ghost boutons) and Syt-4 (number of transient ghost boutons and mEJPs) cargoes to show a minimal dependence on cargo delivery via ESCRT-derived EVs for these cargoes to carry out their synaptic growth and plasticity functions in vivo. However, it should be notes that for Evi/ Wg cargo, there is a slight increase in developmentally-arrested ghost boutons suggesting the cargo may not be entirely independent of EV-mediated cargo delivery. Finally, authors express an anti-GFP proteasome-directed nanobody using motor neuron or muscle-specific drivers and find that Syt4-GFP cargo doesn't enter muscle cytoplasm as fluorescence is maintained and cargo is not degraded by the muscle proteasome. While authors suggest this as evidence of EV-mediated transfer for cargo proteostasis, it is not explicitly shown that Syt4 cargo is, in fact, trafficked and degraded by the lysosome or hypothesized how Syt4 function or post-synaptic localization may be carried out independently of EVs.

Major comments:

• It is difficult to evaluate the findings of this study without knowing the extent of ESCRT pathway impairment. Please provide data quantifying the degree of knockdown/ mutant expression for each ESCRT component (i.e., western blot)
• Loss of ESCRT machinery likely disrupts the release of small EVs to a significant extent; however, the authors do not show that EV release is entirely lost, only that 1) cargoes are backed up in the endosomal system due to endosomal dysfunction and 2) fluorescence of cargoes in the postsynaptic compartment is diminished. To claim that ESCRT-derived EVs with the relevant cargoes are lost, the authors should perform immunogold labelling with TEM. This would provide direct evidence that the cargoes examined here are packaged in ILVs, and that the ILVs are of a size (~50-150nm) consistent with exosomes (which should really be referred to as small extracellular vesicles (sEVs) per the minimal information for studies of extracellular vesicles (MISEV 2018 [https://doi.org/10.1080/20013078.2018.1535750])
• Additionally, EM would show the loss of cargo packaging and provide information about where these cargoes localize in the presence of ESCRT mutants/loss-of-function.
• Other biogenesis pathways utilize multivesicular bodies to generate EVs, most prominently the nSMase2/ceramide synthesis pathway (which operates in an ESCRT-independent manner). It is possible that this pathway compensates when there are defects in the canonical ESCRT pathway. Thus, it is imperative for the authors to show that the cargo secretion no longer occurs in the presence of ESCRT mutations/loss-of-function. The authors should also use nSMase2 pathway mutants to see if the phenotypes in cargo trafficking (i.e., pre/ post-synaptic protein levels) are recapitulated.
• The authors' findings support that cargo trafficking is affected by widespread endosomal dysfunction but doesn't cleanly prove that 1) synaptic sEV release is lost and 2) that cargo-specific sEVs are lost. As previously mentioned, loss of cargo+ ILVs in MVEs by TEM could demonstrate this, but another useful approach would be to include in vitro Drosophila primary neuronal culture/ EV isolation and mass spec/proteomic characterization studies as proof of concept. According to widely agreed upon guidelines in the EV field, the authors should directly characterize their EV population to show 1) the appropriate size distribution associated with exosomes/sEVs, 2) the presence of traditional EV markers (i.e., tetraspanins), 3) changes in overall EV count by ESCRT mutants, and 4) decreased levels of cargo(es) of interest in the presence of ESCRT mutants/loss-of-function. In vitro experiments would be particularly helpful for quantifying the degree of loss of cargo-specific EVs with each ESCRT mutant. These experiments could also investigate the possibility that cargoes are secreted in nSMase2/ Ceramide-derived EVs, by showing that EV cargo levels are unaffected in nSMase mutants.
• During functional tests of Evi+ motor neurons lacking generation of Evi+ EVs, there is a slight defect observed, namely the increased formation of developmentally arrested ghost boutons when Evi secretion in sEVs is lost. As mentioned, Evi is a transporter of Wg and it is possible for Wg to be transmitted between cells via normal diffusion. Thus, some basal levels of Wg may be reaching the muscle when its transfer via sEVs is abolished, and these basal levels may be sufficient to phenocopy the WT in the number of active zones and boutons. Is it possible that this element of Evi/ Wg function is dose-dependent and thus reliant on the extra Evi/ Wg transferred via sEVs? If possible, the authors should use a Wnt-signaling pathway reporter (i.e., fluorescently tagged Beta-Catenin) to measure the levels of Wnt signaling activity in the muscle when Evi/Wg+ EVs are present vs. abolished. If the degree of Wnt signaling (readout would be intensity of fluorescent reporter) is decreased without Evi+ sEVs, there may be a dose-dependent response. Otherwise, please more clearly disclose the partial loss of Evi function without Evi+ sEVs or state the intact function of Evi without sEVs as speculative.
• To support the authors' hypothesis that Syt4 transmission via EVs is a proteostatic mechanism, the authors should determine whether Syt4 cargo localizes to lysosomal compartments in muscle, glia, or both. Otherwise, the proteostatic degradation of Syt4 via EVs is speculative.
• Please discuss alternate modes of cargo transfer from the presynaptic compartment to the postsynaptic compartment that may be utilized when EV-mediated transfer is abolished (i.e., cytonemes or tunneling nanotubules).
• OPTIONAL: Investigate the mechanism of Syt4+ sEV fusion with the postsynaptic compartment (direct fusion with the plasma membrane, receptor-mediated fusion, endocytosis and unpacking, or endocytosis and degradation).
• Given that several fundamental questions have yet to be answered regarding the biogenesis pathways and machinery utilized for EV-mediated cargo secretion, and the necessity for further TEM studies and/or work with primary cultures to characterize ILVs and EVs, >6 months is estimated to perform the necessary experiments that may require learning/ optimizing new systems.

Minor comments:

• Please clarify the choice of using Tsg101 KD in place of mutants of other ESCRT machinery (i.e., Hrs). Especially as when the Tsg101 mutant was characterized, you found major defects in autophagic flux that were not present for HrsD28/Df.
• Please clarify why the specific method in experiment in Fig. 4E-J was chosen. As Syt4 is a transmembrane protein, is likely undergoes degradation via the lysosome, like other membrane-bound proteins. Is it known whether the proteasome-directed nanobody is sufficient to pull Syt4 from membrane-bound compartments to undergo degradation in the proteasome? Would it make more sense to use a lysosome-directed nanobody?
• Please provide further methodological information regarding the sample preparation for live imaging of axons to generate kymographs found in Fig. S3.
• In Figure 1I and 1J, include representative image and quantification of Syt4-GFP pre- and post-synaptic intensity for HrsD28/Df for consistency with ShrubKD and Vps4DN in Figure 1K-P.
• In Figure 2H, please provide a cell type marker or HRP mask with a merged image for image clarity.
• In Figure 4B, please provide quantification for the differences between 1) WT Mock and Tsg101 MOCK and 2) WT Stim and Tsg101KD Stim to show that upon stimulation, WT and Tsg101 undergo the same increase in the number of ghost boutons/ NMJ in Muscle 4.
• In Figure 3 G and H, use consistent scale bars to compare between temperatures.

Significance

General assessment (Strengths):

• Use of Drosophila NMJ model system consistent with others in the field and exceptional harnessing of genetic tools for mutations across the ESCRT pathway (-0, -I, -III, etc.)
• Identification of ESCRT pathway mutants that do not deplete pre-synaptic cargo levels but generate endosomal dysfunction, indicative of a possible decrease in secretion of cargoes via EVs
• Implementing functional characterization of Evi/ Wg and Syt4 cargoes, consistent with previous work in the field; highly reproducible
• Sufficiently thorough investigation of the cross-regulation of autophagy and EV biogenesis by Tsg101

General assessment (Weaknesses):

• Lack of investigation of known ESCRT-independent pathways/ genes involved in the generation of sEVs (i.e., nSMase2/ Ceramide) especially as it is unknown if minor sources of cargo+ EVs are sufficient in maintaining functional phenotype
• Lack of sEV characterization and validation of EVs derived from mutant
• Does not show the loss of cargoes of interest on EVs from mutants other than through back-up of cargoes in the presynaptic endocytic pathway (Rab7, Rab5, Rab11)
• Lack of rigorous investigation of the claim that Evi and Syt4 are released via EVs for proteostatic means is missing. Authors should demonstrate the degradation of EV cargoes by recipient cells (either muscle OR glia)
• If EV-mediated cargo transfer is not required, authors should investigate alternate modes of cargo transfer more rigorously (i.e., diffusion of Wg, suggest/ test hypotheses for mechanism of Syt4 function or transfer).

Advance:

• Compared with other recent in vivo studies of EVs where donor EVs are loaded with a cargo, such as Cre, which uniquely identifies recipient cells through Cre recombination-mediated expression of a fluorescent reporter (Zomer et al 2015, Cell), this study relies on the readout of fluorescently tagged cargo in the recipient cells to represent transfer via EVs. While numerous studies in the Drosophila field focus on the same small set of known EV cargoes at the NMJ (Koles et al., 2012; Gross et al., 2012; Korkut et al., 2013; Korkut et al., 2009; Walsh et al., 2021), there is a noticeable lack of EV characterization based on MISEV (i.e. TEM of EVs, size distribution, enrichment of well-known EV markers [https://doi.org/10.1080/20013078.2018.1535750]) that would significantly strengthen the work and make it more widely accepted in the EV field.
• In this study, the use of ESCRT machinery mutants is proven as a new technical method in delineating the role of EV cargoes in cell-autonomous versus EV-dependent functions. This is the first study, to my knowledge, that has leveraged mutants from both early and late ESCRT complexes for the study of EVs in Drosophila. Additionally, the finding that some cargoes may be able to carry out their signaling functions, independent of transfer via EVs, provides key mechanistic insight into one possible role of EVs as proteostatic shuttles for cargo. This work also begins to address a fundamental question in the field, which is to delineate roles that EVs actually carry out in physiological conditions, compared to the many roles that have been shown possible in vitro.

Audience:

• Basic research (endosomal biology, ESCRT pathway, cell signaling, neurodevelopment)
• Specialized (Drosophila, Neurobiology; Extracellular Vesicles)
• This article will be of interest to basic scientists in the field of endosomal trafficking and extracellular vesicle biology as well as though studying the nervous system in Drosophila melanogaster. As the field of extracellular vesicle biology has broad implications in the spread of pathogenic cargoes in cancer and neurodegenerative disease, the basic biology associated with EVs has some translational relevance.

Expertise (Keywords):

• ESCRT and nSMase2 EV biogenesis pathways
• EV characterization in vitro/ live imaging studies
• EV release and uptake
• Neuronal and glial cell biology

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Reply to the reviewers

1. Point-by-point description of the revisions

__Response to Reviewers’ comments and suggestions __

We are thankful to the reviewers for their time and effort to review our study and for their constructive suggestions. We address below their comments to further improve the manuscript.

__Reviewer #1 __

Major revision points:

The authors should consider using CENH3 as a marker instead of NDC80 to claim NEK1's role in chromosome segregation. Using a direct marker like CENH3 would strengthen their conclusion. However, if the authors choose not to generate the cell line and new set of data, it would be advisable to tone down their conclusion regarding chromosome segregation. I acknowledge the extensive work and data present in the paper.

Response: Thanks to the reviewer for the suggestion. We have tried previously to generate a CENH3-GFP marker line but were not successful. We also requested a CenH3 antibody from the group who published it, but without success. These are the reasons why we generated the NDC80 line, which is another kinetochore marker for chromosome segregation. We have characterised the NDC80-GFP parasite line extensively in a previous study using live cell imaging and super-resolution microscopy to follow its spatiotemporal dynamics at different stages of the Plasmodium life cycle including its correlation with the kinetochore (Zeeshan et al, 2020). We showed its binding to the centromeric region of chromosomes by ChIP seq analysis (See the figure below-Zeeshan et al, 2020). In our recent studies we also showed its dynamic location with other spindle markers like EB1 and ARK2 (Zeeshan et al, 2023). Based on these data, we believe that both CENH3 and NDC80 are appropriate markers for chromosome segregation in Plasmodium, and we hope that the reviewer appreciates this interpretation.

We are pleased to read that the reviewer recognises the extensive amount of work and data present in the paper.

Minor revision points: The figures are well-designed and presented to a high standard. I especially appreciate the guide schematics associated with the IFAs. However, one area that could be improved is the presentation of the expanded parasites. Firstly, the insets cover a major section of the cell, concealing data from the figure. Secondly, the NHS-ester signal is currently saturated and could be dimmed to more accurately represent the MTOC.

Response: We thank the reviewer for their appreciation and suggestions to further improve the figures. We have shifted the insets on the figures to avoid concealing the data. We have tried to improve the NHS-ester signal and provided more Z-stacks to show the MTOC more accurately. Please see the new supplementary figure S7.

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

Major points (please note that both points do not necessarily need further experiments):

1) there is a scarcity for n numbers for many parts of the manuscript. Please give some indications how many cells were inspected, how often a phenotype was observed and how often an experiment was independently carried out (see also minor points).

Response: We have now provided better quantification for all the observations, with the number of cells observed and how many times each experiment was performed reported in the figure legends and in the method section.

2) While the -omics data is interesting, it is somewhat disconnected from the remainder of the manuscript in that it does not lead to any experimental work on the cell level to bring it in connection with NEK1 nor is there any validation. For instance, while the interactome analysis includes a good proportion of very plausible hits, not a single one is validated. I do see that it may be beyond this manuscript to do extensive validations but as this data has limits what can be concluded from it, this should at least be stated in the text. For instance in the paragraph in the discussion (line 613etc). Some experimental validations, if only to show location at the expected site, would be even better.

Response: We thank the reviewer for this insight. We have reanalysed the proteomics data and identified some other MTOC and spindle proteins, including kinesin-8B and kinesin-13 (see new Figure 4). We have already validated kinesin-8B as an MTOC/basal body marker in a previous study, with a similar phenotype during male gametogenesis resulting from its ablation (Zeeshan et al, 2019). Here we show the relative location of NEK1 with respect to that of kinesin-8B, which has a similar MTOC location in early-stage male gametogenesis. In another study we showed that kinesin-13 is localised at the MTOC and spindle and has a similar role during male gametogenesis (Zeeshan et al, 2022). Other proteins, including PF16 and kinesin15, have also been shown to be important for male gametogenesis (Straschil et al, 2010, Zeeshan et al, 2022).

Minor points: 1) Plasmodium is a species name, better not use it on its own (Anopheles would also not be used on its own if Anopheles mosquitoes are meant).

Response: We now mentioned the particular species of the Plasmodium genus or in general, we use Plasmodium spp.

2) While the imaging is very nice, I do have some issues with backgrounds containing mostly pixels of zero intensity (which seems to be the case for some of the images). In western blots this is not permitted anymore (because it is unclear what was clipped and whether this made weaker bands disappear). The same should apply to microscopy, unless very specific and defined analyses were used that caused this. If this was the case here (e.g. deconvolution, back ground subtraction etc), this should be stated for each type of imaging (including parameters). If this was just due to adjusting levels in Photoshp to clip low intensity, I would recommend to reduce that to a degree where no pixel has 0 intensity anymore to ensure no information in the image was lost.

Response: We thank the reviewer for pointing out this issue. Here, we have used several different types of imaging, including live cell, structural illumination microscopy (SIM), expansion microscopy and fixed immunofluorescence. In general, we adjusted the backgrounds for most of these images as necessary but did not use photoshop for any of them. For live cell imaging, the GFP/RFP fluorescent cell signals are well captured at different time points with an auto-exposure time and then processed simply using Axiovision/Zeiss zen software. SIM images were captured using different parameters based on fluorescence signal intensity and processed to remove background at a threshold level. We provide the processing parameters in the SIM processing method section). For expansion microscopy (ExM), the Z stacks were collected for different channels and the brightness adjusted to remove background. The SIM and ExM resolution images are presented as maximum intensity projections, as explained in the methods section; please see pages 23, 25 and 27. An example of SIM image processing is shown below:

3) Line 158: The role of NEK1 in centrosome splitting in Toxoplasma. Given that Plasmodium NEKs are not analogous to mammalian NEKs, a quick word on the relation of Plasmodium and Toxoplasma NEKs may be beneficial. Does Toxo also have 4 NEKs and is TgNEK1 an orthologoue of Plasmodium NEK1?

Response: In fact, Toxoplasma gondii encodes 4 NEKs (Miranda-Saavedra et al., 2012; PMID: 22587893), with TgNEK1 the orthologue of Plasmodium spp NEK1.

4) Fig. S1A: is hDHFR really fused to NEK1? Maybe the scheme can be updated to clarify this without readers having to consult the cited publication (Guttery et al., 2014a)

Response: We apologise for the confusion; we have updated and clarified the schematic for readers.

5) Line 135: those other model eukaryotes -> insert "of" before other

Response: We thank the reviewer for spotting this error and have now inserted “of”.

6) Line 149: is substituted by an SMASH -> by a SMASH

Response: We thank the reviewer for spotting this error and have now substituted by “a SMASH”.

7) Line 151: in the modulation of MAPK pathway -> an article seems to be missing here

Response: We thank the reviewer for pointing out the missing article and have now added Dorin-Semblat et al., 2007 article on MAP kinases to the text.

8) Line 153: remove first bracket

Response: We thank the reviewer for noticing the surplus bracket which has now been removed.

9) Line 189; insert „the" before parasite life cycle

Response: We thank the reviewer for noticing this and have now inserted “the”.

10) Line 211: We observed an overlap of NEK1 and centrin signals but in this case NEK1 was closer than centrin to the DNA (Fig 1C). In contrast to the NDC80 statement ("NDC80-mCherry was always closer to the DNA"), there is no quantitative information. Looking at the images this also seems a bit less clear cut. Can the authors put a number to his in some way?

Response: We thank the reviewer for highlighting this issue. To clarify, we have added some images showing the locations of Centrin-4/NDC80/DNA (New Fig 1B). We also calculated the overlap of DNA with centrin and DNA with NEK1 in the images showing the signals of these proteins (new Fig 1E). Similarly, the overlap of DNA with Ndc80 and DNA with NEK1 was calculated in the images showing the signals of these proteins (new Fig 1F). This analysis describes the order of signals for the different markers showing centrin is further than NDC80 from the DNA.

11) Line 216: The live cell images of the proliferative liver schizogony (Fig S1D) and sporogony (Fig S1E) stages showed similar patterns of NEK1-GFP foci formation during proliferative stages. Can the authors specify what they mean with similar? I do not see any change from cytoplasmic to one focus per nucleus in the liver schizont and also in sporogony there only seems one focus per nucleus in the sporozoite.

Response: The focal points are not very clear in these stages. Plasmodium liver and oocyst stages contain thousands of progenies and accurate study of the temporal dynamics of GFP expression is difficult. We highlight here that NEK1-GFP is localised at focal points in the nucleus, together with a diffused cytoplasmic location similar to that in asexual blood and male gametocyte stages. These foci are only observed during proliferative stages in cells undergoing active endomitosis in both oocyst and liver stages. No signal is observed in later stages when nuclear division is finished.

12) Not all videos seem to have been treated the same way. Video 1 shows strong increase in the DAPI signal, suggesting post-acquisition boosting of the signal in later time points to compensate for GFP bleaching. In contrast the DAPI in Video S2 stays in a reasonable dynamic range. Can the type of processing used be indicated in the materials or legends?

Response: We agree with the reviewer. Our main aim here was to observe the dynamic location of GFP- and RFP-tagged proteins at various stages during male gametogenesis, and not focus on quantifying the signal. We adjusted different channels according to fluorescence intensity only to show the protein location. We could collect a series of timelapse images for only two to three minutes because the GFP/RFP signals are bleached quickly.

13) Particularly for Fig. 2F and Fig. S2, Fig. 3I-L and Fig. 6A but also for others, please indicate how many cells and independent experiments this is based on and give the number in the legend (image representative of X inspected cells or something along these lines). Fig. 6B has some of that information in the main text but also their total number of cells inspected should be added to the figure legend.

Response: We thank the reviewer for this important suggestion. We now include the total number of cells analysed for each representative image, and the number of experiments performed, in both the figure legends and methods section.

14) Line318/Figure 3: "Live cell imaging showed that both NEK1 and kinesin-8B were located in the cytoplasm (Fig 3G, S3D)". And also later in this paragraph: Fig. S3D should be S3G and S3H. Also, the recruitment of Kinesin-8B within the first 30 seconds that is mentioned is not shown, a pre-induction image would be generally good to show. At the start of video 6 Kinesin-8B is also already recruited.

Response: We thank the reviewer for this suggestion. We have now included pre-induction gametocytes images showing expression of these proteins in new Fig 3A.

15) Line 339: "the" before nucleus might make this long sentence clearer.

Response: We thank the reviewer for pointing this out. “the” has now been added.

16) Line 341: Fig. 3I, beaded NDC80 signal. This signal does not seem that much different to some of the other markers in the SIM images in this figure part and the signal looks quite processed. How sure are the authors that the beads are real? This would be a very fascinating data point, so maybe worth providing some more image data. Does the number of NDC80 foci make sense? See also point 13.

Response: We thank the reviewer for pointing out this observation. We agree that that the NDC80 signal in this image does not look disimilar from some others, but this beaded structure is present in many images we have captured. Our focus was to locate the NEK1 signal relative to the signal of NDC80, and it was very challenging to capture both focal points, especially using two markers. We have replaced the image in Fig 3I with another with better signals for NDC80 and included more images in supplementary figures (S3I and J) to validate the observation. In previous studies we have observed similar NDC80 foci (about 28 NDC80 foci in a diploid gametocyte). (Zeeshan et al 2022 and Zeeshan et al 2023); please see the following figure. The NDC80 focal points represent the number of unclustered kinetochores; for example, in a diploid gametocyte during spindle formation, this would be expected for the Plasmodium haploid genome consisting of 14 chromosomes and the centromeric region of each chromosome associated with the kinetochore multi-protein complex that facilitates spindle attachment.

17) Is S4A a replicate of Fig. 5A, it looks like the identical gel? Was this done more than once? Maybe also add that it was a 1 h induction time into the figure. Three replicates were done for the qPCR for the clag promoter strategy, but again this graph is in both, Fig. 5 and Fig. S4. Can the authors weed out the redundancies in these two figures and provide all n numbers?

Response: We thank the reviewer for highlighting this duplication of the image to show depletion/downregulation of NEK1. The image that was originally part of main Figure 5 has now been deleted, leaving it in supplementary Figure S4.

18) Line 419: please help the reader here and modify to start of this paragraph with something along the lines of "To generate PTD lines..."

Response: We have modified the start of the sentence to make clear to readers the importance of the PTD lines.

19) Line 432: Is this how this is typically phrased (In mosquitoes fed NEK1clag parasites)? I would remove "s" from mosquitoes or insert "with" after "fed" (or maybe fed on NEK1clag infected mice?).

Response: We thank the reviewer for this suggestion. We have added “with” after “fed”.

20) Line 436: on the naïve mice, remove "the"

Response: We thank the reviewer for noticing this. We have removed “the” before naïve mice.

21) Line 446: log2fold -1.5

Response: We thank the reviewer for pointing this out and have corrected this.

22) Fig. S5: It might be beneficial to give in the figure the information to at a glance see what kind of data the figure parts show because it is a mix of RNASeq, phosphoproteomics, NEK1clag and NEK1-AID/HA gametocytes.

Response: We thank the reviewer for this suggestion and have now described the data/plots showing RNA-seq and phosphoproteomic analyses in Figure S5.

23) Line 500: consider replacing imaging with information.

Response: We thank the reviewer for this suggestion and have now replaced “imaging” with “information”.

24) Line 585: remove "be"

Response: We thank the reviewer for spotting this and have now removed “be”.

25) Not all symbol fonts did survive PDF conversion, see e.g. line 1050 or 1101 or 1197.

Response: We are not quite sure why the symbols did not survive conversion to pdf; we have tested conversion of the Word file to pdf format and all the symbols survived.

Reviewer #2 (Significance (Required)):

The strength of this work is the very comprehensive imaging data that combines several high-end techniques and provides a coherent picture. It has all the necessary markers to firstly localize NEK1 in the context of mitosis and then understand the phenotype when it is inactivated. The weakness of this work lies in the limited quantitative information on some of the observed phenotypes.

Response: We appreciate the concern of the reviewer and have revised the manuscript by adding further quantitative information in figure legends and in the method section.

and in the limited pursuit of the findings of the -omics data although, in favour of the paper - these data do add meaningfully to the overall picture even if they were not further validated.

Response: We have discussed more about the omics data. Please line number 656-58 in discussion

__Reviewer #3 __

Major comments:

1. NEK1 mutant parasites show a defect in male gametogenesis. Did authors observe any defect on female gamete formation? This data can be included in the main manuscript. An IFA with female gametocyte marker such as Pbg337 can be included to demonstrate sex-specific expression of NEK1. Response: We have investigated sex-specificity by using P28 antibody (13.1), a reagent which is generally used in P. berghei to identify female gametes and zygotes (we do not have a Pbg337-specific reagent and assume that the reviewer is referring to Pf g377). We see no defect in the number of female gametes formed and identified by surface expression of P28 (Fig S4I and J). This observation was supported by the lack of NEK1-GFP expression in female gametocytes at any time point (Fig. S1F). Furthermore, the rescue experiment (now added in Fig 5F) proves that the defect is only in the male and not the female lineage.

Authors should include genetic crosses experiments to demonstrate female gametes of NEK1 mutant are fertile. Authors appear to have sex-sterile lines available in their lab and have performed these experiments in their previous studies (PMID: 37704606).

Response: We thank the reviewer for this suggestion. We have now performed the genetic rescue experiment by crossing NEK1Clag parasites with two female deficient lines (Δnek4 and Δdozi) and one male deficient line (Δhap2). In three independent set of experiments, we could rescue the defect in NEK1Clag parasites by crossing with female deficient lines, but not by crossing with the male deficient line, by observing ookinete formation. These data are presented in Fig 5F.

1. Proteomic and phosphoproteomic data using mutant NEK1 parasites showed differential phosphorylation of several proteins but authors did not observe same proteins to be differentially phosphorylated in different replicates. Using in vitro experiments involving peptides or recombinant protein fragments, authors should validate and demonstrate some of the substrates to be direct parasite substrates for NEK1. Kinesin-15 can be one good candidate substrate as kinesin-15 is less phosphorylated in NEK1-AID/HA and is enriched in NEK1-GFP Immunoprecipitates. This is very relevant especially since authors observe perturbation of levels for several other kinases in NEK1 knock down parasites.

Response: We appreciate the reviewer’s suggestion to do in vitro biochemical experimentation to validate NEK1 kinase substrates. With respect, this suggestion is well beyond the focus of this study since our aim was to characterise the cell biology of NEK1 function in vivo, with a focus on male gametogenesis. Kinesin-15 together with NEK1 was one of the few proteins for which we detected a significant reduction of phosphorylated peptides across all replicates, despite the high sample variability (likely linked to the pre-treatment involving ethanol and/or auxin to degrade the auxin-induced degron). It is therefore highly likely that phosphorylation of Kinesin-15-S454 is dependent on NEK1. We observed no differential phosphorylation of other kinases in the dataset, but we cannot exclude that other kinases or phosphatases are involved in this signalling pathway.

NEK1 is known to phosphorylate MAP2 kinase in vitro in P. falciparum. Did authors find MAP2 to be differentially phosphorylated in their dataset? It should be discussed accordingly in the current manuscript.

Response: We observed phosphorylation of serine 301 in MAPK2. At 6 min post-activation we detected a two-fold reduction of the corresponding peptide with a Q-value of 0.0528, which is just above the selected threshold. Given the high replicate variability, it is possible that this serine is phosphorylated by NEK1 upon gametocyte activation, but more targeted analyses would be necessary to test this hypothesis. As this observation is still rather speculative, we preferred to refer to it in the discussion.

1. Authors show that NEK1 is expressed in pre-erythrocytic stages. Since authors have multiple tools/ transgenic parasites to study relative expression of NEK1, authors can test relative expression of NEK1 in pre-erythrocytic stages and discuss possible function of NEK1 during liver stages.

Response: We appreciate this suggestion of the reviewer, but we consider the proposed work to be outside the scope of this manuscript, where our focus is on the role of NEK1 in sexual cells. We agree that it will be interesting to examine the possible function of NEK1 in liver stages and believe that several groups are now embarking upon such work.

Minor comments: Authors should cite relevant literature on role of kinases in male gametogenesis by adding a paragraph. e.g. PMID: 18532880, PMID: 29042501, PMID: 29311293, PMID: 32568069, PMID: 34724830, PMID: 32681115, PMID: 36154191 and other kinases.

Response: These references have been added in the discussion section, line numbers 632-635.

Reviewer #3 (Significance (Required)):

Expansion microscopy and live cell imaging are cutting edge and provide the detail and dynamic picture of NEK1 expression in the context of components associated with rapid mitosis, spindle formation, and Kinetochore attachment. This study adds new information to our understanding of the process of male gametogenesis in apicomplexan parasites.

Response: We appreciate these encouraging comments.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Zeeshan et al. investigates the function of Never in mitosis (NIMA)-like kinase (NEK 1) during Plasmodium gametogenesis with a focus on NEK1 in the rodent malaria parasites. The current study shows NEK1 as an important component present near MTOC, kinetochore complex and assisting in spindle formation during rapid mitosis during gametogenesis. Using NEK1-GFP parasites, authors show general association of NEK1 with axoneme/ciliary proteins as well as subunits of the replication machinery. By conditional knock down approaches, authors showed that NEK1 is required during male gametogenesis and parasite transmission to mosquitoes suggesting it to be a significant target for developing transmission blocking interventions.

Major comments:

1. NEK1 mutant parasites show a defect in male gametogenesis. Did authors observe any defect on female gamete formation? This data can be included in the main manuscript. . An IFA with female gametocyte marker such as Pbg337 can be included to demonstrate sex-specific expression of NEK1.
2. Authors should include genetic crosses experiments to demonstrate female gametes of NEK1 mutant are fertile. Authors appear to have sex-sterile lines available in their lab and have performed these experiments in their previous studies (PMID: 37704606).
3. Proteomic and phosphoproteomic data using mutant NEK1 parasites showed differential phosphorylation of several proteins but authors did not observe same proteins to be differentially phosphorylated in different replicates. Using in vitro experiments involving peptides or recombinant protein fragments, authors should validate and demonstrate some of the substrates to be direct parasite substrates for NEK1. Kinesin-15 can be one good candidate substrate as kinesin-15 is less phosphorylated in NEK1-AID/HA and is enriched in NEK1-GFP Immunoprecipitates. This is very relevant especially since authors observe perturbation of levels for several other kinases in NEK1 knock down parasites.
4. NEK1 is known to phosphorylate MAP2 kinase in vitro in P. falciparum. Did authors find MAP2 to be differentially phosphorylated in their dataset? It should be discussed accordingly in the current manuscript.
5. Authors show that NEK1 is expressed in pre-erythrocytic stages. Since authors have multiple tools/ transgenic parasites to study relative expression of NEK1, authors can test relative expression of NEK1 in pre-erythrocytic stages and discuss possible function of NEK1 during liver stages.

Minor comments:

Authors should cite relevant literature on role of kinases in male gametogenesis by adding a paragraph. e.g. PMID: 18532880, PMID: 29042501, PMID: 29311293, PMID: 32568069, PMID: 34724830, PMID: 32681115, PMID: 36154191 and other kinases.

Significance

Expansion microscopy and live cell imaging are cutting edge and provide the detail and dynamic picture of NEK1 expression in the context of components associated with rapid mitosis, spindle formation, and Kinetochore attachment. This study adds new information to our understanding of the process of male gametogenesis in apicomplexan parasites.

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Referee #2

Evidence, reproducibility and clarity

A fascinating aspect of malaria parasite biology is the incredibly fast generation of 8 nuclei in microgamete formation. In this work the authors identify NEK1, one of the 4 NEKs of the parasite, as an essential protein in that process. They use impressive imaging (but see small comment on that below) including live cell time lapse, superresolution, expansion and EM with markers to describe the location of NEK1 in relation to mitosis relevant structures and the impact of its loss. This is bolstered by some IP, RNASeq and phosphoproteomic data, providing a very thorough characterization of NEK1 although these data are less thorough than the imaging. The sound conclusion from the authors is that Nek1 is needed for MTOC organization, spindle assembly and kinetochore attachment in mitosis during male gamete formation.

Major points(please note that both points do not necessarily need further experiments):

1. there is a scarcity for n numbers for many parts of the manuscript. Please give some indications how many cells were inspected, how often a phenotype was observed and how often an experiment was independently carried out (see also minor points).
2. while the -omics data is interesting, it is somewhat disconnected from the remainder of the manuscript in that it does not lead to any experimental work on the cell level to bring it in connection with NEK1 nor is there any validation. For instance, while the interactome analysis includes a good proportion of very plausible hits, not a single one is validated. I do see that it may be beyond this manuscript to do extensive validations but as this data has limits what can be concluded from it, this should at least be stated in the text. For instance in the paragraph in the discussion (line 613etc). Some experimental validations, if only to show location at the expected site, would be even better.

Minor points:

1. Plasmodium is a species name, better not use it on its own (Anopheles would also not be used on its own if Anopheles mosquitoes are meant).
2. While the imaging is very nice, I do have some issues with backgrounds containing mostly pixels of zero intensity (which seems to be the case for some of the images). In western blots this is not permitted anymore (because it is unclear what was clipped and whether this made weaker bands disappear). The same should apply to microscopy, unless very specific and defined analyses were used that caused this. If this was the case here (e.g. deconvolution, back ground subtraction etc), this should be stated for each type of imaging (including parameters). If this was just due to adjusting levels in Photoshp to clip low intensity, I would recommend to reduce that to a degree where no pixel has 0 intensity anymore to ensure no information in the image was lost.
3. Line 158: The role of NEK1 in centrosome splitting in Toxoplasma. Given that Plasmodium NEKs are not analogous to mammalian NEKs, a quick word on the relation of Plasmodium and Toxoplasma NEKs may be beneficial. Does Toxo also have 4 NEKs and is TgNEK1 an orthologoue of Plasmodium NEK1?
4. Fig. S1A: is hDHFR really fused to NEK1? Maybe the scheme can be updated to clarify this without readers having to consult the cited publication (Guttery et al., 2014a)
5. Line 135: those other model eukaryotes -> insert "of" before other
6. Line 149: is substituted by an SMASH -> by a SMASH
7. Line 151: in the modulation of MAPK pathway -> an article seems to be missing here
8. Line 153: remove first bracket
9. Line 189; insert „the" before parasite life cycle
10. Line 211: We observed an overlap of NEK1 and centrin signals but in this case NEK1 was closer than centrin to the DNA (Fig 1C). In contrast to the NDC80 statement ("NDC80-mCherry was always closer to the DNA"), there is no quantitative information. Looking at the images this also seems a bit less clear cut. Can the authors put a number to his in some way?
11. Line 216: The live cell images of the proliferative liver schizogony (Fig S1D) and sporogony (Fig S1E) stages showed similar patterns of NEK1-GFP foci formation during proliferative stages. Can the authors specify what they mean with similar? I do not see any change from cytoplasmic to one focus per nucleus in the liver schizont and also in sporogony there only seems one focus per nucleus in the sporozoite.
12. Not all videos seem to have been treated the same way. Video 1 shows strong increase in the DAPI signal, suggesting post acquisition boosting of the signal in later time points to compensate for GFP bleaching. In contrast the DAPI in Video S2 stays in a reasonable dynamic range. Can the type of processing used be indicated in the materials or legends?
13. Particularly for Fig. 2F and Fig. S2, Fig. 3I-L and Fig. 6A but also for others, please indicate how many cells and independent experiments this is based on and give the number in the legend (image representative of X inspected cells or something along these lines). Fig. 6B has some of that information in the main text but also there total number of cells inspected should be added to the figure legend.
14. Line318/Figure 3: "Live cell imaging showed that both NEK1 and kinesin-8B were located in the cytoplasm (Fig 3G, S3D)". And also later in this paragraph: Fig. S3D should be S3G and S3H. Also, the recruitment of Kinesin-8B within the first 30 seconds that is mentioned is not shown, a pre-induction image would be generally good to show. At the start of video 6 Kinesin-8B is also already recruited.
15. Line 339: "the" before nucleus might make this long sentence clearer.
16. Line 341: Fig. 3I, beaded NDC80 signal. This signal does not seem that much different to some of the other markers in the SIM images in this figure part and the signal looks quite processed. How sure are the authors that the beads are real? This would be a very fascinating data point, so maybe worth providing some more image data. Does the number of NDC80 foci make sense? See also point 13.
17. Is S4A a replicate of Fig. 5A, it looks like the identical gel? Was this done more than once? Maybe also add that it was a 1 h induction time into the figure. Three replicates were done for the qPCR for the clag promoter strategy, but again this graph is in both, Fig. 5 and Fig. S4. Can the authors weed out the redundancies in these two figures and provide all n numbers?
18. Line 419: please help the reader here and modify to start of this paragraph with something along the lines of "To generate PTD lines..."
19. Line 432: Is this how this is typically phrased (In mosquitoes fed NEK1clag parasites)? I would remove "s" from mosquitoes or insert "with" after "fed" (or maybe fed on NEK1clag infected mice?).
20. Line 436: on the naïve mice, remove "the"
21. Line 446: log2fold 1.5 likely should be log2fold>-1.5
22. Fig. S5: It might be beneficial to give in the figure the information to at a glance see what kind of data the figure parts show because it is a mix of RNASeq, phosphoproteomics, NEK1clag and NEK1-AID/HA gametocytes.
23. Line 500: consider replacing imaging with information.
24. Line 585: remove "be"
25. Not all symbol fonts did survive PDF conversion, see e.g. line 1050 or 1101 or 1197.

Significance

The strength of this work is the very comprehensive imaging data that combines several high-end techniques and provides a coherent picture. It has all the necessary markers to firstly localize NEK1 in the context of mitosis and then understand the phenotype when it is inactivated. The weakness of this work lies in the limited quantitative information on some of the observed phenotypes and in the limited pursuit of the findings of the -omics data although, in favour of the paper - these data do add meaningfully to the overall picture even if they were not further validated.

The study provides very interesting information to a field that currently is gaining momentum in malaria research. It will be of interest to researchers working on

• mitosis in malaria parasites and other apicomplexans
• kinases in these parasites and likely also for researchers working on mitosis in model organisms.

Expertise: I am a cell biologist working with P. falciparum blood stages

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Referee #1

Evidence, reproducibility and clarity

Summary:

This article by Zeeshan et al. investigates the role of NEK1 kinase in Plasmodium, the malaria parasite, focusing on its essential functions in microtubule organizing center (MTOC) organization and kinetochore attachment during the rapid mitosis involved in male gamete formation. Utilizing a combination of live cell imaging, ultrastructure expansion microscopy (U-ExM), and various molecular biology techniques, the authors elucidate the spatiotemporal dynamics of NEK1 in relation to MTOC dynamics across different stages of the Plasmodium life cycle. Their findings reveal that NEK1 is crucial for coordinating spindle formation and chromosome segregation, highlighting its potential as a target for malaria intervention strategies.

Strengths:

Comprehensive Methodological Approach: The combination of cutting-edge imaging techniques with conditional gene knockdown and proteomics provides a robust framework for investigating NEK1's role in Plasmodium mitosis, ensuring the reliability and depth of the findings. Novel Insights into Plasmodium Biology: The study offers groundbreaking insights into the mitotic mechanisms of Plasmodium, particularly the atypical processes involved in male gametogenesis, thereby filling a significant knowledge gap. Implications for Malaria Control: By identifying a potential new drug target, this research directly contributes to the ongoing malaria control and eradication efforts, highlighting the translational potential of basic biological research. Major revision points: The authors should consider using CENH3 as a marker instead of NDC80 to claim NEK1's role in chromosome segregation. Using a direct marker like CENH3 would strengthen their conclusion. However, if the authors choose not to generate the cell line and new set of data, it would be advisable to tone down their conclusion regarding chromosome segregation. I acknowledge the extensive work and data present in the paper. Minor revision points: The figures are well-designed and presented to a high standard. I especially appreciate the guide schematics associated with the IFAs. However, one area that could be improved is the presentation of the expanded parasites. Firstly, the insets cover a major section of the cell, concealing data from the figure. Secondly, the NHS-ester signal is currently saturated and could be dimmed to more accurately represent the MTOC.

Significance

This study significantly advances our understanding of the cell cycle mechanisms in Plasmodium, particularly the unique mitotic processes involved in male gametogenesis. By elucidating the role of NEK1 kinase, the research addresses a critical gap in malaria biology, offering insights into the parasite's ability to proliferate and transmit between hosts. The identification of NEK1 as a key regulator of MTOC organization and kinetochore attachment during Plasmodium mitosis not only broadens our fundamental knowledge of cellular division in divergent eukaryotes. The study lays a solid foundation for future research to disrupt malaria transmission through targeted intervention strategies. Further exploration of NEK1's interactions and the development of specific inhibitors could pave the way for novel antimalarial therapies, highlighting the importance of continued research in this area.

The article by Zeeshan et al. contributes significantly to our understanding of Plasmodium biology, particularly the role of NEK1 kinase in the parasite's cell cycle. Despite some limitations, such as the scope of kinase investigation and the direct translation to therapeutic applications, the study lays a solid foundation for future research to disrupt malaria transmission through targeted intervention strategies. Further exploration of NEK1's interactions and the development of specific inhibitors could pave the way for novel antimalarial therapies, highlighting the importance of continued research in this area.

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Reply to the reviewers

Response to reviewer comments

R: We really appreciate the reviewer positive comments and consideration, and we believe that the review process has significantly strengthened our manuscript.

We have responded to all the reviewer comments, as follows:

Response (R)

FROM REVIEWER #1

Major comments:

The manuscript is mostly well written (it could use a few minor grammatical corrections), the significance of the problem is well described, and the results are clearly presented with adequate controls. The movies, provided as supplementary material, are of the highest quality and are essential additions to the stills provided in the figures. The data convincingly support the key conclusions of the manuscript.

R: We sincerely appreciate the positive comments provided by the reviewer. In response, we have thoroughly revised the manuscript to address any grammatical issue.

Does the MO knockdown both S and L homeologs of X. laevis? Since the level of GAPDH in Figure 1H also looks reduced in Gai2 MO lane, it should be made clear that the apparent knockdown of Gai2 was normalized to GAPDH, rather than being the results of unequal loading of the gel. Yes, I recognize that Figure 1I says normalized, but this is not stated in the results or the methods. Also, was this experiment done with X. laevis or X. tropicalis? I could imagine that if done in X. laevis, the lack of complete knockdown might be due to only one homeolog being affected.

R: We appreciate the reviewer comment, and we described in Material and Methods section the region targeted by the morpholino, in both Xenopus species. We added the next paragraph in the Material and Methods section, see page 24, paragraph 2, lines: 4-11:

"MO against Xenopus Gαi2 was designed by GeneTools to target the 5' UTR site of X. tropicalis (X.t) and X. laevis (X.l) transcripts (Gαi2MO: 5'-CGACACAGCCCCAGATAGTGCGT-3'). Specifically, it hybridizes with the 5' UTR of X. t Gαi2 (NM_203919), 17 nucleotides upstream of the ATG start codon. For X. l Gαi2, the morpholino hybridizes with both isoforms described in Xenbase. It specifically targets the 5' UTR of the Gαi2.L isoform (XM_018258962), located 17 nucleotides upstream of the ATG start codon, and the 5' UTR of the Gαi2.S isoform (NM_001097056), situated 275 nucleotides upstream of the ATG."

With respect to Figure 1H and 1I, we have specified in the Fig. 1 legend that we normalized the data to GAPDH to quantifying the decrease in Gαi2 expression induced by the morpholino.

See page 40, Figure 1H-I, Legends section. Finally, the result showed in Fig. 1A-I was done in X.t., that was now stated at the legend from the figure. We added at the Supplementary material Fig.1S, the result done in X.l. experiment.

The knowledge of the efficacy of knockdown in each Xenopus species provided by the information requested in the previous point, would allow the reader to assess the level of knockdown in the remaining assays. To do this, the authors should tell us which assays were done in which species. I am not suggesting that each experiment needs to be done in each species, only that the information should be provided. If the MO is more effective in X. tropicalis - which assays used this species? If the knock down is partial, as shown in Figure 1H-I, which species this represents in the remaining assays would be useful knowledge.

R: We greatly appreciate the reviewer's valuable comments and suggestions, and as a response, we have incorporated a new supplementary figure (Figure S1). This figure includes a western blot and an in situ hybridization assay illustrating the efficiency of the knockdown in Xenopus laevis. The results presented in Figure S1 demonstrate that the knockdown efficiency is similar in both Xenopus species, allowing for a comparison between Figure 1A-I (X. tropicalis) and Figure 1S (X. laevis).

To complement this information, we have also improved the section of Material and Methods regarding the experiments in both Xenopus species (Xenopus tropicalis and Xenopus laevis). As detailed in the Materials and Methods section, we employed 20 ng of Gai2MO for Xenopus tropicalis embryos and 35 ng of Gai2MO for Xenopus laevis embryos to deplete cell migration. In both species, in vivo migration was analyzed, resulting in a substantial inhibition of cranial neural crest (NC) migration, ranging from 60% to 80%. Additionally, we conducted dispersion assays in both species. In X. laevis, in vitro migration was monitored for 10 hours, while in X. tropicalis, it was tracked for 4 hours, both yielding the same phenotype. We also studied cell morphology and microtubule dynamics in both Xenopus models. However, we used different tracer concentrations for each, with 200 pg for X. laevis and 100 pg for X. tropicalis, as specified in the Materials and Methods section. Our Rac1 and RhoA timelapse experiments were conducted in both species as well, employing pGBD-GFP and rGBD-mCherry probes, respectively, and different probe concentrations as outlined in the Materials and Methods section. These experiments revealed polarity impairment and consistent Rac1 behavior in both Xenopus species. The study of focal adhesion in vivo dynamics using the FAK-GFP tracer was carried out also in both species, resulting in the same phenotype. It is worth noting that the only experiment conducted exclusively in X. tropicalis was the focal adhesion disassembly assay with nocodazole.

Regarding the improvements of the Materials and Method section see page 24, paragraph 1.

We want to highlight that at the beginning of the Materials and Methods section, we incorporated a paragraph to clarify that "All experiments were conducted in both Xenopus species (X.t and X.l) using distinct concentrations of the morpholino (MO) and mRNA, as specified in each respective methodology description". This approach consistently yielded similar results. It is important to note that for the figures, we selected the most representative images.

We have also specified in each figure legend which Xenopus species is depicted.

Minor comments:

While prior studies are referenced appropriately, and the text and figures are mostly clear and accurately presented, the following are a few suggestions that would help the authors improve the presentation of their data and conclusions:

The cell biological experiments convincingly demonstrate that knockdown of Gai2 causes cells to move more slowly. It would be a nice addition to bring the explant experimental data back to the embryo by showing whether the slower moving NC cells in morphants eventually populate the BA. DO they cease to migrate or are they just slower getting to their destination? This could be done by performing snail2 ISH at a later stage (34-35?).

R: We appreciate the reviewer's insightful point, and in response, we conducted the in situ hybridization assay at stages 32-36 to address this question. The result has been included in Figure S1F-H, revealing a delayed migration of cranial neural crest cells. Consequently, we have updated the text in the results section, page 6, paragraph 1, line 18:

"In later developmental stages, such as stage 32, WISH revealed alterations in migration as well, albeit to a lesser extent compared to the early stages (22-23). This suggests a phenotype characterized by delayed migration (supplementary material Fig S1F-H)."

There are places in the manuscript where the authors use the terms "silencing" or "suppression" of Gai2, when they really mean reduced translation - their system is not a genetic knockout, as clearly demonstrated in Figure 1H-I. I suggest that more accurate wording be used.

R: We appreciate the reviewer's comment, and we agree that the Gαi2 morpholino impedes Gαi2 translation, leading to a reduction in Gαi2 protein expression. Consequently, we have revised the entire manuscript, replacing the terms "silencing" and "suppression" with "knockdown".

In Figures 1-5 there are scale of bars on the cell images, but these are not defined in any of the figure legends.

R: We value the reviewer's comment, and we have revised all the figure legends by including the scale information. Each image has been scaled to 10 µm with varying magnifications.

The abstract is the weakest section of the manuscript, and would have greater impact if it were more clearly written.

R: We appreciate the reviewer's comment on the abstract, and we have revised and edited it to enhance its quality.

Abstract:

"Cell migration is a complex and essential process in various biological contexts, from embryonic development to tissue repair and cancer metastasis. Central to this process are the actin and tubulin cytoskeletons, which control cell morphology, polarity, focal adhesion dynamics, and overall motility in response to diverse chemical and mechanical cues. Despite the well- established involvement of heterotrimeric G proteins in cell migration, the precise underlying mechanism remains elusive, particularly in the context of development. This study explores the involvement of Gαi2, a subunit of heterotrimeric G proteins, in cranial neural crest cell migration, a critical event in embryonic development. Our research uncovers the intricate mechanisms underlying Gαi2 influence, revealing a direct interaction with the microtubule-associated protein EB1, and through this with tubulin, suggesting a regulatory function in microtubule dynamics modulation. Here, we show that Gαi2 knockdown leads to microtubule stabilization, alterations in cell polarity and morphology with an increased Rac1-GTP concentration at the leading edge and cell-cell contacts, impaired cortical actin localization and focal adhesion disassembly. Interestingly, in Gai2 depleted cells RhoA-GTP was found to be reduced at cell-cell contacts and concentrated at the leading edge, providing evidence of Gαi2 significant role in polarity. Remarkably, treatment with nocodazole, a microtubule-depolymerizing agent, effectively reduces Rac1 activity, restoring cranial NC cell morphology, actin distribution, and overall migration. Collectively, our findings shed light on the intricate molecular mechanisms underlying cranial neural crest cell migration and highlight the pivotal role of Gαi2 in orchestrating microtubule dynamics through EB1 and EB3 interaction, modulating Rac1 activity during this crucial developmental process."

Reviewer #1 (Significance (Required)):

The molecular regulation of cell movement is a key feature of a number of developmental and homeostatic processes. While many of the proteins involved have been identified, how they interact to provide motility has not been elucidated in any great detail, particularly in embryo-derived cells (as opposed to cell lines). The results obtained from the presented experiments are novel, in-depth and provide a novel paradigm for how G proteins regulate microtubule dynamics which in turn regulate other components of the cytoskeleton required for cell movement. The results will be applicable to many migrating cell types, not just neural crest cells.

Because of the application of the data to many types of cells that migrate, the audience is expected to include a broad array of developmental biologists, basic cell biologists and those interested in clinically relevant aberrant cell migrations.

R: We really appreciate the reviewer positive comments and consideration

FROM REVIEWER #2

Reviewer: Major comments:

The authors aim to address two issues in this manuscript: a) the role of Gai2 in neural crest development; and b) the mechanism of Gai2 function. While they have done a good job demonstrating a role of Gai2 in NC migration both in vivo and in vitro as well as the effects of Gai2 knockdown on cytoskeleton dynamics, protein distribution of selected polarity and focal adhesion molecules, and Rac1 activation, the link between Gai2 and the downstream effectors is largely correlative. Because of this, the model suggesting the sequential events flowing from Gai2 to microtubule to Rac1 to focal adhesion/actin should be modified to allow room for direct and indirect regulation at potentially multiple entry points.

R: We appreciate the valuable comments provided by the reviewer. To further elucidate the mechanism underlying Gαi2 regulation of cranial neural crest cell migration, we have incorporated new data from interaction analysis conducted by PLA (proximity ligand assay). This analysis supports our proposed model, indicating Gαi2 interacts with EB proteins to form a complex with tubulin, thereby regulating microtubules dynamics and subsequently influencing Rac1 and RhoA activity, cell morphology (actin cytoskeleton) and cell-matrix adhesion, ultimately affecting migration. However, we cannot exclude that this regulation may also involve other intermediary proteins, such as GEFs, GAPs, GDIs, and others. Finally, as a result, we have revised our model and its description to provide a more detailed explanation of the potential mechanism in line with the reviewer suggestion. Specifically, we have edited the discussion/conclusion, model and the legend for Figure 6. Please refer to page 16 (paragraph 1, 2 and 3), 22 (paragraph 1), 23 (paragraph 1), 44 (Legend Fig. 6).

__Reviewer: __Specific major comments are as the following:

Strengths:

-Determination of a role of Gai2 in neural crest migration is novel.

-The effect of Gai2 knockdown on membrane protrusion morphology and microtubule stability and dynamics are demonstrated nicely.

-Quantification of experimental perimeters has been performed throughout the manuscript in all the figures, and statistical analysis is included in the figures.

R: We appreciate the reviewer positive comments

Weaknesses: -The heavy focus of the study on microtubule is due to the previous publication on the function of Gai2 in regulation of microtubule during asymmetrical cell division. However, the activity of Gai2 is likely cell type-specific, as it has not been shown to control microtubule during cytokinesis in general. It is equally likely that Gai2 primarily regulates Rac1 or actin regulators to influence both microtubule and actin dynamics. The tone of the discussion should therefore be softened.

R: We greatly appreciate and agree with the comment from the reviewer, highlighting the possibility that Gαi2 primarily regulates Rac1 or actin regulators to influence both microtubule and actin dynamics. In this regard, we have revised our manuscript to include a discussion of this point. We added the next paragraph in the Discussion/Conclusion section, page 22-23.

"It is well established that the activity from the Rho family of small GTPases is controlling cytoskeletal organization during migration (Ridley et al., 2015). Contrariwise, it has been described in many cell types, that microtubules dynamic polymerization plays a crucial role in establishing the structural foundation for cell polarization, consequently influencing the direction of cell motility (Watanabe et al., 2005). Our results appear to align with this latter view. While it is reasonable to postulate the possibility that Gαi2 regulates Rac1 activity, subsequently influencing actin and microtubule dynamics, our findings in the context of cranial NC cells, lend support to an alternative sequence of events. Initially, Gαi2 knockdown leads to a decrease in microtubule dynamics, which in turn increase Rac-GTP towards the leading edge. This shift is accompanied by reduced levels of cortical actin and impaired focal adhesion disassembly, culminating in compromised cell migration. Notably, nocodazole, a microtubule-depolymerizing agent, not only diminishes Rac-GTP localization at the leading edge but also rescues cell morphology, restores normal cortical actin localization, and promotes focal adhesion disassembly, thereby facilitating cell migration. If Rac1 activity were indeed upstream of microtubules, it would be expected that nocodazole would not reduce Rac-GTP levels at the cell leading edge. These results suggest that the regulation of Rac1 activity may follow, rather than precede, alterations in microtubule dynamics, in the context of NC cells. Furthermore, in support of our model, our protein interaction analysis demonstrates Gαi2 interacting with microtubule components such as EB proteins and tubulin. As we already mention above, earlier studies have reported that microtubule dynamics promote Rac1 signaling at the leading edge and by releasing RhoGEFs promote RhoA signaling as well (Best et al., 1996; Garcin and Straube, 2019; Moore et al., 2013; Waterman-Storer et al., 1999). In addition, it is well-documented that RhoGEFs interact with microtubules, including bPix, a GEF for Rac1 and Cdc42, which, in turn, promotes tubulin acetylation (Kwon et al., 2020). Interestingly, in ovarian cancer cells, Gαi2 has been shown to activate Rac1 through an interaction with bPix, thereby jointly regulating migration in response to LPA (Ward et al., 2015). Taken together, these findings further support our proposed model (refer to Fig. 6)."

The effect of rescue of NC migration with Rac1 inhibitor is marginal and the result is hard to interpret considering the inhibitor also blocks control NC migration. Either lower doses of Rac1 inhibitor can be used or the experiment can be removed from the manuscript, as Rac1 is required for membrane protrusions and the inhibitor doses can be hard to titrate.

R: We appreciate and agree with the reviewer's comments. To address this concern and enhance clarity, we have incorporated the following paragraph into the manuscript within the Discussion section. Additionally, we have included information on the range of NSC23766 concentrations used for this analysis in the Materials and Methods section. Page 25, Explants and microdissection.

In the results section see page 11 and 12, paragraph 2.

"It is worth noting that we conducted Rac inhibitor NSC23766 trials at concentrations ranging from 20 nM to 50 nM for X. laevis and between 10 nM to 30 nM for X. tropicalis. In both cases, higher concentrations of the Rac inhibitor proved to be lethal (data not shown), underscoring the essential role of Rac1 in both cell migration and cell survival. Remarkably, our results show partial restoration in cranial NC cells dispersion following a 5-minute treatment with a low concentration of the Rac1 inhibitor (20 nM of NSC23766 X. laevis and 10 nM for X. tropicalis) (Fig. 3L-P, supplementary material movie S5). This suggests that these concentrations are sufficient to demonstrate that the increase in Rac1-GTP resulting from Gαi2 morpholino knockdown impairs cell migration."

The partial rescue can be attributed to the crucial role of microtubule dynamics in cell migration, which acts upstream of Rac activity. Additionally, Rac is pivotal for the modulation of cell polarity at the leading edge of migration. It is worth emphasizing that Rac1 levels are critical for cell migration, as demonstrated by other researchers. Lower concentrations of Rac1-GTP have been shown to hinder cell migration in cells deficient in Rac1, leading to a significant reduction in wound closure and random cell migration (Steffen et al., 2013).

"Therefore, we believe that the lower concentration of NSC23766 used in our assay was adequate to reduce the abnormal Rac1-GTP activity in the morphant NC cells. However, it is important to note that for normal NC cell, this level of reduction in Rac1-GTP activity is critical and sufficient to impair normal migration".

See page 11 and 12, paragraph 2.

Steffen A, Ladwein M, Dimchev GA, Hein A, Schwenkmezger L, Arens S, Ladwein KI, Margit Holleboom J, Schur F, Victor Small J, Schwarz J, Gerhard R, Faix J, Stradal TE, Brakebusch C, Rottner K. Rac function is crucial for cell migration but is not required for spreading and focal adhesion formation. J Cell Sci. 2013 Oct 15;126(Pt 20):4572-88. doi: 10.1242/jcs.118232. Epub 2013 Jul 31. PMID: 23902686; PMCID: PMC3817791.

Since the defects seem to result partially from the inability of the NC cells to retract and move away, it may help to either include some data on Rho activation patterns in knockdown cells or simply add some discussion about the issue.

R: We acknowledge and sincerely appreciate the reviewer's valuable comments on this pivotal aspect, which significantly enhances our capacity to elucidate the impact of Gαi2 knockdown on cell polarity. To address this crucial point, we have introduced an experiment that examines RhoA-GTP localization under Gαi2 knockdown conditions, and we have incorporated a supplementary figure S3 into our manuscript. This newly added figure clearly demonstrates that, under Gαi2 knockdown conditions, and in contrast to control cells, RhoA-GTP localization is substantially disrupted at cell-cell contacts and now detected at the leading edge of the cell, providing compelling evidence of cell polarity defects (refer to Figure S3A-C). In response to these results, we have included a description of these findings in the Results section (please see page 10) and a dedicated paragraph in the Discussion section (please see page 19, paragraph 2, last line, page 19-21).

Results section 1 (page 10, paragraph 1 line 6-12): "To achieve this, we explored whether Gαi2 regulates the subcellular distribution of active Rac1 and RhoA in cranial NC explants under Gαi2 loss-of-function conditions, considering their pivotal roles in cranial NC migration and contact inhibition of locomotion (CIL) (Carmona-Fontaine et al., 2011; Moore et al., 2013; Leal et al., 2018). Hence, we employed mRNA encoding the small GTPase-based probe, enabling specific visualization of the GTP-bound states of these proteins."

Results section 2 (page 10, paragraph 1 line 14-27): "Consistent with earlier observations by Carmona-Fontaine et al. (2011), in control cranial NC cells, active Rac1 displayed prominent localization at the leading edge of migrating cells, whereas its presence was reduced at cell-cell contacts, coincident with an increase in RhoA-GTP levels (white arrows in Fig. 3A, supplementary material Figure S3A,C). On the contrary, in comparison to the control cells, Gαi2 morphants exhibit a pronounced accumulation of active Rac1 protein in the protrusions at cell-cell contacts, where active RhoA localization is conventionally expected (white arrow in Fig. 4B, supplementary material Figure S3A,C and movie S4). In contrast to control cells, a notable shift in the localization of active RhoA protein was observed, with its predominant accumulation now detected at the leading edge of the cell, instead of the typical localization towards the trailing edge or cell-cell contacts (__supplementary material Figure S3B,C). __These findings suggest a dysregulation of contractile forces that align with the observed distribution of active RhoA, cortical actin disruption, and diminished retraction in cell treated with Gαi2MO."

*Discussion section: (page 19 last line, page 20, paragraph 1, line 1-20) *

"Other studies have reported that microtubule assembly promotes Rac1 signaling at the leading edge, while microtubule depolymerization stimulates RhoA signaling through guanine nucleotide exchange factors associated with microtubule-binding proteins controlling cell contractility, via Rho-ROCK and focal adhesion formation (Krendel et al., 2002; Ren et al., 1999; Best et al., 1996; Garcin and Straube, 2019; Waterman-Storer et al., 1999; Bershadsky et al., 1996; Moore et al., 2013). This mechanism would contribute to establishing the antero-posterior polarity of cells, crucial for maintaining migration directionality, underscoring the significance of regulating microtubule dynamics in directed cell migration. These findings closely align with the results obtained in this investigation, demonstrating that Gαi2 loss of function reduces microtubule catastrophes and promotes tubulin stabilization, resulting in increased localization of active Rac1 at the leading edge and cell-cell contacts, while decreasing active RhoA at the cell-cell contact but increasing it at the leading edge. This possibly reinforces focal adhesion, which is consistent with the presence of large and highly stable focal adhesions under Gαi2 knockdown conditions. This finding also suggests a dysregulation of contractile forces in comparison to control cells, a result that aligns with the observed distribution of active RhoA, cortical actin distribution and diminished retraction in cells treated with Gαi2MO. This strikingly contrasts with the normal cranial NC migration phenotype, where Rac1 is suppressed while active RhoA is increased at cell-cell contacts during CIL, leading to a shift in polarity towards the cell-free edge to sustain directed migration (Theveneau et al., 2010; Shoval and Kalcheim, 2012; Leal et al., 2018)."

To consider focal adhesion dynamics, live imaging should be used in the analysis. The fixed samples are different from each other, and natural variations of focal adhesion may exist among the samples. This can obscure data collection and quantification.

R: We agree with the reviewer that focal adhesion (FA) dynamics need to be analysed using live imaging. Indeed, Fig 5E-H shows an extensive analysis of FA using live imaging of neural crest expressing FAK-GFP. As complement to this live imaging analysis, and in order to analyse the effect on the endogenous levels of FA proteins, we performed immunostaining against FA. Both experiments using live imaging or fixed cells produce similar results, and they are consistent with our model on the role of Gαi2 on FA dynamics.

Reviewer: minor comments

Fig. 2, the centrosomes in control cells are not always obvious. The microtubules simply seem to be more networked and more fluid in control cells. This should be clarified with either marking the centrosomes in the figure or modifying the wording in the manuscript.

R: We appreciate and concur with the reviewer's comment on this matter. As pointed out by the reviewer, the precise localization of the centrosome is not consistently clear in all cells. In response to this observation, we have revised the manuscript to emphasize this aspect solely as "microtubule morphology". Please refer to the Results section description Figure 2.

In Fig. 3, a better negative control for co-IP should be using anti-V5 antibody to IP against tubulin/EB1/EB3 in the absence of Gai2-V5.

R: We appreciate the reviewer's comment, and we agree with the suggested control. Accordingly, we have included this control in Supplementary material Figure S4A. Additionally, we conducted all Co-IPP in triplicate, and these data have been incorporated into Supplementary material Figure S4B. Furthermore, as mentioned earlier, we have reorganized some of the sections of the results to improve the logical flow of the manuscript's description. As a result, the Figure presenting the interaction analysis by Co-IPP now corresponds to Figure 5.

The data for cell polarity proteins Par3 and PKC-zeta seem to be out of place. It is unclear whether mis-localization of these proteins has anything to do with NC migration defects induced by Gai2 knockdown. The conclusion does not seem to be affected if the data are taken out of the manuscript.

R: We appreciate the reviewer's concern, and we would like to highlight two points in this regard. Firstly, we have included these results as additional data to support the impact of Gai2 knockdown on cell polarity, given that these two proteins are commonly used as polarity markers. Secondly, we have discussed this aspect extensively in the Discussion section of the manuscript. (See page 20, paragraph 1, lines 21-31).

In that section, we delve into the relationship between aPKC, Par3, and Gαi2 in controlling cell polarity during asymmetric cell division, as described in Hao et al., 2010. Par3 is known to play a role in regulating microtubule dynamics and Rac1 activation through its interaction with Rac-GEF Tiam1 (Chen et al., 2005). Additionally, it has been shown to promote microtubule catastrophes and inhibit Rac1/Trio signaling, regulating Contact Inhibition of Locomotion (CIL) as demonstrated in Moore et al., 2013. Thus, we believe that the data we present support the relationship between Par3 and aPKC localization changes and the neural crest migration defects induced by Gαi2 knockdown, probably by controlling microtubule dynamics. However, we have moved these results as part of the supplementary Figure S3D-G.

In Suppl. Fig. 1, protrusion versus retraction should be defined more clearly. The retraction shown in this figure seems to be just membrane between protrusions instead of actively retracting membrane.

R: We appreciate the reviewer's comments, and here we aim to provide a clearer description of our approach to this analysis. For the measurement of protrusion extension/retraction, we conducted two distinct experiments. The first, as described in Figure 1, involved measuring membrane extension and retraction in live cell using membrane-GFP by utilizing the image subtraction tool in ImageJ, which highlights changes in the membrane in red. Secondly, we employed ADAPT software to quantify cell perimeter based on fluorescence intensity in live cell using lifeactin-GFP, distinguishing membrane extension in green and retraction in red (as has been shown similarly in Barry et al., 2015). In both approaches, we observed a substantial increase in membrane protrusion (both in area and extension) and protrusion stability in Gαi2 morphants. Hence, we have revised the Materials and Methods section of the manuscript and included this clarification.

See Materials and Methods section, Cell dispersion and morphology, page 28.

In addition we inform hat this images now are included in Supplementary material Fig S2G,H.

Barry DJ, Durkin CH, Abella JV, Way M. Open source software for quantification of cell migration, protrusions and fluorescence intensities. J Cell Biol. 2015. Doi: 10.1083/jcb.201501081

Discussion can be improved by better incorporating all the components to make a cohesive story on how Gai2 works to regulate migration in the context of the neural crest cells.

R: We appreciate the reviewer's comment and agree. To enhance the manuscript, we have included a new paragraph at the end of the Discussion/Conclusion section specifically addressing this point. For more details, please refer to page 23.

"Therefore, in the context of collective cranial NC cells migration, our findings reveal the pivotal role played by Gαi2 in orchestrating the intricate interplay of microtubule dynamics and cellular polarity. When Gαi2 levels are diminished, we observe significant impediments in the ability of cells to efficiently navigate through their environment, resulting in a range of distinct effects. First and foremost, Gαi2 deficiency leads to the diminished ability of cells to adjust and reorient new protrusions effectively. Primary protrusions exhibit higher stability and heightened levels of active Rac1/RhoA when compared to control conditions in the leading edge. In addition, we observe a notable increase in protrusion area, a decrease in retraction velocity, and an enhanced level of cell-matrix adhesion in Gαi2 knockdown cells. These findings underscore the pivotal role that Gαi2 plays in the modulation of various cellular dynamics essential for collective cranial NC cells migration. Notably, the application of nocodazole, a microtubule-depolymerizing agent, and NSC73266, a Rac1 inhibitor, to Gαi2 knockdown cells leads to the rescue of the observed effects, thus facilitating migration. This observed response closely mirrors the outcomes associated with Par3, a known regulator of microtubule catastrophe during contact inhibition of locomotion (CIL) in NC cells (Moore et al., 2013). This parallel implies that there exists a delicate equilibrium between microtubule dynamics and Rac1-GTP levels, crucial for the establishment of proper cell polarity during collective migration. Our findings collectively position Gαi2 as a central master regulator within the intricate framework of collective cranial NC migration. This master regulator role is pivotal in orchestrating the dynamics of polarity, morphology, and cell-matrix adhesion by modulating microtubule dynamics through interactions with EB1 and EB3 proteins, described here for the first time, possible in a protein complex involving other intermediary proteins such as other microtubules accessory proteins like CLIP170, actin intermediaries, like mDia1-2, and signaling proteins such as GDIs, GAPs and GEFs, thus fostering crosstalk between the actin and tubulin cytoskeletons. This orchestration ultimately ensures the effective collective migration of cranial NC cells (Fig. 6)."

Review____er #2 (Significance (Required)):

The authors demonstrate a role of Gai2 in regulation of neural crest migration in Xenopus by modulating microtubule dynamics. In addition, they show an effect of Gai2 knockdown on Rac1 spatial activation and focal adhesion stability. These are novel discoveries of the study. Some limitations exist in linking Gai2 with downstream effectors that directly or indirectly impact on cytoskeleton and Rac1 small GTPase.

R: We really appreciate the reviewer positive comments and consideration. We believe that the review process has significantly strengthened our manuscript in this regard.

FROM REVIEWER #3

__ ____Reviewer: mayor comments:__

The authors focus exclusively on the analysis of the subcellular levels of Rac1, which is probably related to the fact that they observe large extended protrusions with high Rac1 activity. However, as the authors note, a global fine-tuning of Rho GTPase activity is required for neural crest migration. One of the observed phenotypes of Gαi2-morphant neural crest cells is a decrease in cell dispersion, which may be caused by defects in contact inhibition of locomotion (CIL). This process involves a local activation of RhoA at cell-cell contact sites (Carmona-Fontaine et al., 2008). Furthermore, in fibroblast, RhoA/ROCK activity is required for the front-rear polarity switch during CIL (Kadir et al., 2011). Interestingly, similar to the Gαi2 loss of function phenotype, ROCK inhibition leads to microtubule stabilization, which can be rescued by nocodazole treatment, restoring microtubule dynamics and CIL. Therefore, it would also be interesting to know how RhoA activity is affected in Gαi2-morphant NC cells. At a minimum, this point should be be included in the discussion.

R: We acknowledge and sincerely appreciate the reviewer's valuable comments on this pivotal aspect, which significantly enhances our capacity to elucidate the impact of Gαi2 knockdown on cell polarity. To address this crucial point, we have introduced an experiment that examines RhoA-GTP localization under Gαi2 knockdown conditions, and we have incorporated a supplementary figure S3A-C into our manuscript. This newly added figure clearly demonstrates that, under Gαi2 knockdown conditions and in contrast to control cells, RhoA-GTP localization is substantially disrupted at cell-cell contacts and now detected at the leading edge of the cell, providing compelling evidence of cell polarity defects (refer to Figure S3). In response to these results, we have included a description of these findings in the Results section (please see page 10) and a dedicated paragraph in the Discussion section (please see page 19-20).

Results section 1 (page 10, paragraph 1 line 6-12): "To achieve this, we explored whether Gαi2 regulates the subcellular distribution of active Rac1 and RhoA in cranial NC explants under Gαi2 loss-of-function conditions, considering their pivotal roles in cranial NC migration and contact inhibition of locomotion (CIL) (Carmona-Fontaine et al., 2011; Moore et al., 2013; Leal et al., 2018). Hence, we employed mRNA encoding the small GTPase-based probe, enabling specific visualization of the GTP-bound states of these proteins."

Results section 2 (page 10, paragraph 1 line 14-27): "Consistent with earlier observations by Carmona-Fontaine et al. (2011), in control cranial NC cells, active Rac1 displayed prominent localization at the leading edge of migrating cells, whereas its presence was reduced at cell-cell contacts, coincident with an increase in RhoA-GTP levels (white arrows in Fig. 3A, supplementary material Figure S3A,C). On the contrary, in comparison to the control cells, Gαi2 morphants exhibit a pronounced accumulation of active Rac1 protein in the protrusions at cell-cell contacts, where active RhoA localization is conventionally expected (white arrow in Fig. 4B, supplementary material Figure S3A,C and movie S4). In contrast to control cells, a notable shift in the localization of active RhoA protein was observed, with its predominant accumulation now detected at the leading edge of the cell, instead of the typical localization towards the trailing edge or cell-cell contacts (__supplementary material Figure S3B,C). __These findings suggest a dysregulation of contractile forces that align with the observed distribution of active RhoA, cortical actin disruption, and diminished retraction in cell treated with Gαi2MO."

*Discussion section: (page 19, second paragraph, line 12 and page 20, paragraph 1, line 1-18) *

"Other studies have reported that microtubule assembly promotes Rac1 signaling at the leading edge, while microtubule depolymerization stimulates RhoA signaling through guanine nucleotide exchange factors associated with microtubule-binding proteins controlling cell contractility, via Rho-ROCK and focal adhesion formation (Krendel et al., 2002; Ren et al., 1999; Best et al., 1996; Garcin and Straube, 2019; Waterman-Storer et al., 1999; Bershadsky et al., 1996; Moore et al., 2013). This mechanism would contribute to establishing the antero-posterior polarity of cells, crucial for maintaining migration directionality, underscoring the significance of regulating microtubule dynamics in directed cell migration. These findings closely align with the results obtained in this investigation, demonstrating that Gαi2 loss of function reduces microtubule catastrophes and promotes tubulin stabilization, resulting in increased localization of active Rac1 at the leading edge and cell-cell contacts, while decreasing active RhoA at the cell-cell contact but increasing it at the leading edge. This possibly reinforces focal adhesion, which is consistent with the presence of large and highly stable focal adhesions under Gαi2 knockdown conditions. This finding also suggests a dysregulation of contractile forces in comparison to control cells, a result that aligns with the observed distribution of active RhoA, cortical actin distribution and diminished retraction in cells treated with Gαi2MO. This strikingly contrasts with the normal cranial NC migration phenotype, where Rac1 is suppressed while active RhoA is increased at cell-cell contacts during CIL, leading to a shift in polarity towards the cell-free edge to sustain directed migration (Theveneau et al., 2010; Shoval and Kalcheim, 2012; Leal et al., 2018)."

The co-Immunoprecipitation data lack marker bands (larger images/sections of the blots would be preferable) and the labelling is not clear. What do the white arrows in Fig. 3H,I mean? What does "elu" and "non eluted" mean?. ? Did the reverse IP work as well?

R: We appreciate the reviewer's comments, and here we intend to provide a more detailed explanation of our approach to this analysis. Since we do not possess a secondary antibody specific to the heavy chain, our method involves eluting the co-immunoprecipitated proteins to visualize those with weights close to that of the light chain (such as EB1). We have outlined this elution step in the "Cell lysates and co-immunoprecipitation" protocol in the Materials and Methods section. To ensure proper control, we load both fractions - the eluted (or supernatant) and non-eluted (or resin) fractions - to monitor the amount of protein extracted from the resin using a 1% SDS solution. It's important to note that the elution step, as indicated by the V5 signal, is not entirely efficient, and a significant portion of the protein remains bound to the resin. This issue may also apply to the EB1 protein; however, it is still possible to visualize both bands (Gαi2V5 and EB1).

As we mentioned earlier the Co-IPP analysis now are in Figure 5. We have revised the legend for Figure 5 to include an explanation of the terms 'elu' (eluted fraction) and 'non-eluted' (non-eluted fraction). We have also included the explanation of the white arrows' significance in the legends for Figure 5H and 5I. These arrows indicate the bands corresponding to the immunoprecipitated proteins.

We also agree with the reviewer's suggestion to conduct the reverse IP. To address this point, and in favour of the lack of this control, accordingly, we have included a negative control for co-IP using anti-V5 antibody to IP, this control was included in Supplementary material Figure S4A. Additionally, we conducted all Co-IPP in triplicate, and these data have been incorporated into Supplementary material Figure S4B.

The presentation of the Delaunay triangulations varies in quality. In Fig. 1 J/K the cells are clearly visible in the images, while this is not the case in Fig. 3 J-M and Fig. 4K-N. Conversely, the Delaunay triangulations in Fig. 1L are mainly black, while they are clear in Fig. 3 and 4. Perhaps the authors could find a more consistent way to present the data. Were the explants all approximately the same size at the beginning of the experiment? The Gαi2-morphant explant in Fig. 3K appears to be unusually small.

R: We appreciate the reviewer's concerns and have taken steps to address them. To improve the quality of our data, we have made enhancements to the presentation of Figures 3 (panels L-O) and Figure 5 (panels P-S). Specifically, we have standardized the Delaunay triangulation representations.

Regarding the size of the explants at the beginning of the experiments, they were indeed approximately similar in size. We confirmed this by including a reference point (point 0) for each condition in the figures 5. However, in the panels presented, we show the results after 10 hours (Figure 5, X. laevis, in the actual Figure organization) and 4 hours (Figure 3, X. tropicalis, in the actual Figure organization) to assess cell dispersion, as indicated in the respective figure legends. This uniformity in size was further ensured by the calculation used to quantify dispersion. For the dispersion assay, we normalized each initial size of the explant upon the control, and we have added another representative explant of Gαi2 morpholino with its Delaunay triangulation to facilitate the experiment interpretation. Every Delaunay triangulation calculates the area generated between three adjacent cells and it grows depending on how much disperse are the cells between each other in the final point. (See Material and Methods section, Cell dispersion and morphology). As we can see in the manuscript, in every dispersion experiment that we have performed with Gαi2 morpholino, the cells cannot disperse at all. Furthermore, to analyze the dispersion rate in this experiment we use Control n= 21 explants, Gαi2MO n= 24 explants, Gαi2MO + 65 nM Nocodazole n= 36 explants, Control + 65 nM Nocodazole n= 30 explants (as we mentioned in the manuscript legend).

Why was the tubulin distribution in Fig. 2F measured from the nucleus to the cell cortex? Would it not make more sense to include cell protrusions? This does not seem to be the case in the example shown in Fig. 2F.

R: We appreciate the reviewer's concern. We would like to clarify that for the tubulin distribution measurements, we indeed measured from the nucleus to the cell protrusion. As a result, we have made an edit to Figure 2 (panel 2F) to provide further clarity on this matter.

The immunostaining for acetylated tubulin (Fig. 3A,B) looks potentially unspecific and seems to co-localize with actin (for comparison see Bance et al., 2019). For imaging and quantification, it may be better to use tubulin co-staining to calculate the percentage of acetylated tubulin. Please also add marker bands to the Western blot in Fig. 3C. If this issue cannot be resolved it may be better to only include the Western blot data.

R: We appreciate the reviewer's concern about the potential unspecific nature of acetylated-tubulin and its co-localization with actin. Regarding the co-localization with actin, it is predominantly observed in panel B, and we attribute this phenomenon to the Gαi2 morphant phenotype, where cortical actin is notably reduced, creating the appearance of co-localization. In response to the reviewer comment, we have retained the acetylated tubulin western blot analysis in the main Figure 5A,B, while relocating the immunofluorescence analysis to Supplementary material Figure S4C-H. Additionally, we have included the measurements of the acetylated tubulin fluorescence intensity for both conditions Gαi2MO and control, as depicted Supplementary material Figure S4I.

We have also included marker weight indications on the western blot panel in now Figure 5A.

The model in Fig.6 indicates that Gαi2 inhibits EB1/3. What is the experimental evidence and the proposed mechanism for this? In the discussion, the authors cite evidence that Gαi activates the intrinsic GTPase activity of tubulin, which would destabilize microtubules by removing the GTP cap. However, this mechanism would not directly affect EB1 and EB3 stability as the Fig. 6A seems to suggest. The authors also mention that EB3 appears to be permanently associated with microtubules in Gαi2-morphant cells. How would this work, given that end-binding proteins bind to the cap region? Are the authors suggesting that there is an extended cap region in Gαi2 morphants?

R: We appreciate the reviewer's valuable comments. We have revised our model accordingly to our data and new data that we have incorporated regarding interaction analysis conducted by PLA (proximity ligand assay), in order to further elucidate the mechanism underlying Gαi2 regulation of cranial neural crest cell migration. This analysis supports our actual proposed model, indicating Gαi2 interacts with EB proteins to form a complex with tubulin, thereby regulating microtubules dynamics and subsequently influencing Rac1 and RhoA activity, cell morphology (actin cytoskeleton) and cell-matrix adhesion, ultimately affecting migration. Therefore, we have revised our model and its description to provide a more detailed explanation of the potential mechanism in line with the reviewer suggestion. Specifically, we have edited the discussion/conclusion, model and the legend for Figure 6. Please refer to page 16 (paragraph 1, 2 and 3), 22 (paragraph 1), 23 (paragraph 1), 45 (Legend Fig. 6). In addition, in Gαi2 knockdown conditions we have found a strong reduction in microtubules dynamics following EB3-GFP comets. Regarding the observation that EB3 seems to be persistently associated with microtubules in Gαi2-morphant cells, we wish to clarify that this is a speculation based on the microtubule phenotype observed during our dynamic analysis, where they appear more like lines rather than comets. It is important to note that none of the experiments conducted in this study conclusively demonstrate this, and thus, it remains a suggestion. As a result, we have revised our model in accordance with the reviewer suggestion.

Reviewer 3: minor comments:

The citation of Wang et al. 2018 in the introduction does not seem to fit.

R: We appreciate the correction provided by the reviewer. We have carefully reviewed the Introduction and Reference sections and have corrected this error.

Does the graph in Fig. 4S show average values for the three conditions? If so, what is the standard deviation?

R: We appreciate the reviewer's concern and we have added the standard deviation to now Figure 4J.

From the images in Fig. 2G and H, it is difficult to understand what the difference is between the four groups shown.

R: We appreciate the reviewer's comment, and to clarify this point, we would like to explain that the comparison has been made between each type of comet. The PlusTipTracker software separates comets based on their speed and lifetime, classifying them as fast long-lived, fast short-lived, slow long-lived, or slow short-lived. In both conditions (control and morphant cells), we compared the percentage of each type of comet, as previously described in Moore et al., 2013. The results demonstrate that morphant cells exhibit an increase in slow comets compared to control cells. The same explanation is described in the Material and Methods section on page 28, Microtubule dynamics analysis.

Review____er #3: (Significance (Required)):

Overall, the study is well executed and significantly advances our understanding of the control and role of microtubule dynamics in cell migration, which is much less understood compared to the function of the actin cytoskeleton in this process. The strength of the study is the use of state-of-the-art (live imaging) techniques to characterize the role of Gαi in neural crest migration at the cellular/subcellular level. This article will be of interest to a broad readership, including researchers interested in basic embryonic morphogenesis, cell migration, and cytoskeletal dynamics, as well as translational/clinical researchers interested in cancer progression or wound healing.

R: We really appreciate the reviewer positive comments and consideration. We believe that the review process has significantly strengthened our manuscript.

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

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Referee #3

Evidence, reproducibility and clarity

Summary: The manuscript by Villaseca et al. analyzes the role of Gαi2 in cranial neural crest migration and reveals a novel mechanistic link to microtubule dynamics. The authors nicely demonstrate that Gαi2 is required for Xenopus neural crest migration and affects cell dispersion, cell polarity, focal adhesion turnover, and microtubule dynamics. They find that Gαi2-morphant neural crest cells are elongated, have larger, more stable protrusions, higher active Rac1 levels, and a concentration of microtubules at the leading edge. Using co-immunoprecipitation, the authors show that Gαi2 forms a complex with α-tubulin and the microtubule plus-end binding proteins EB1 and EB3, which are known regulators of microtubule dynamics. Time-lapse imaging shows that Gαi2 loss of function increases microtubule stability, which is further supported by an increase in acetylated tubulin levels. Consistently, treatment with nocodazole, which inhibits microtubule polymerization, as well as treatment with a Rac1 inhibitor, is able to rescue cell dispersion and morphology of Gαi2-morphant neural crest cells. The authors propose a model, whereby Gαi2 interacts with components of the plus-tip microtubule-binding complex to control microtubule dynamics and Rac1 activity to establish cell polarity, disassemble focal adhesion, and thereby facilitate neural crest migration.

Major comments:

1. The authors focus exclusively on the analysis of the subcellular levels of Rac1, which is probably related to the fact that they observe large extended protrusions with high Rac1 activity. However, as the authors note, a global fine-tuning of Rho GTPase activity is required for neural crest migration. One of the observed phenotypes of Gαi2-morphant neural crest cells is a decrease in cell dispersion, which may be caused by defects in contact inhibition of locomotion (CIL). This process involves a local activation of RhoA at cell-cell contact sites (Carmona-Fontaine et al., 2008). Furthermore, in fibroblast, RhoA/ROCK activity is required for the front-rear polarity switch during CIL (Kadir et al., 2011). Interestingly, similar to the Gαi2 loss of function phenotype, ROCK inhibition leads to microtubule stabilization, which can be rescued by nocodazole treatment, restoring microtubule dynamics and CIL. Therefore, it would also be interesting to know how RhoA activity is affected in Gαi2-morphant NC cells. At a minimum, this point should be be included in the discussion.
2. The co-Immunoprecipitation data lack marker bands (larger images/sections of the blots would be preferable) and the labelling is not clear. What do the white arrows in Fig. 3H,I mean? What does "elu" and "non eluted" mean? Did the reverse IP work as well?
3. The presentation of the Delaunay triangulations varies in quality. In Fig. 1 J/K the cells are clearly visible in the images, while this is not the case in Fig. 3 J-M and Fig. 4K-N. Conversely, the Delaunay triangulations in Fig. 1L are mainly black, while they are clear in Fig. 3 and 4. Perhaps the authors could find a more consistent way to present the data. Were the explants all approximately the same size at the beginning of the experiment? The Gαi2-morphant explant in Fig. 3K appears to be unusually small.
4. Why was the tubulin distribution in Fig. 2F measured from the nucleus to the cell cortex? Would it not make more sense to include cell protrusions? This does not seem to be the case in the example shown in Fig. 2F.
5. The immunostaining for acetylated tubulin (Fig. 3A,B) looks potentially unspecific and seems to co-localize with actin (for comparison see Bance et al., 2019). For imaging and quantification, it may be better to use tubulin co-staining to calculate the percentage of acetylated tubulin. Please also add marker bands to the Western blot in Fig. 3C. If this issue cannot be resolved it may be better to only include the Western blot data.
6. The model in Fig.6 indicates that Gαi2 inhibits EB1/3. What is the experimental evidence and the proposed mechanism for this? In the discussion, the authors cite evidence that Gαi activates the intrinsic GTPase activity of tubulin, which would destabilize microtubules by removing the GTP cap. However, this mechanism would not directly affect EB1 and EB3 stability as the Fig. 6A seems to suggest. The authors also mention that EB3 appears to be permanently associated with microtubules in Gαi2-morphant cells. How would this work, given that end-binding proteins bind to the cap region? Are the authors suggesting that there is an extended cap region in Gαi2 morphants?

Minor comments

1. The citation of Wang et al. 2018 in the introduction does not seem to fit.
2. Does the graph in Fig. 4S show average values for the three conditions? If so, what is the standard deviation?
3. From the images in Fig. 2G and H, it is difficult to understand what the difference is between the four groups shown.

Referees cross-commenting The concerns raised by my colleagues are entirely valid.

Significance

Overall, the study is well executed and significantly advances our understanding of the control and role of microtubule dynamics in cell migration, which is much less understood compared to the function of the actin cytoskeleton in this process. The strength of the study is the use of state-of-the-art (live imaging) techniques to characterize the role of Gαi in neural crest migration at the cellular/subcellular level. This article will be of interest to a broad readership, including researchers interested in basic embryonic morphogenesis, cell migration, and cytoskeletal dynamics, as well as translational/clinical researchers interested in cancer progression or wound healing.

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Referee #2

Evidence, reproducibility and clarity

Summary

The manuscript by Villaseca et al. describes functional analysis of Gai2 in cranial neural crest (CNC) migration using the frog Xenopus as their model system. The authors performed the loss-of-function assay to knock down expression of endogenous of Gai2 and discovered that CNC migration was impaired in the absence of changes of CNC fate specification. Based on the literature on Gai2 activities in other cellular contexts, the authors speculated that Gai2 might regulate microtubule dynamics and Rac1 function. Their studies using immunofluorescence (IF) and live-cell imaging indeed showed that microtubules were stabilized in membrane protrusions with concurrent activation of Rac1 in Gai2 knockdown cells. In addition, focal adhesion turnover was reduced. They further demonstrated that the CNC migration defects could be partially rescued by destabilization of microtubules with chemical treatment. The authors conclude from the studies that Gai2 orchestrates microtubule dynamics and modulates Rac1 activation during neural crest migration.

Major comments

The authors aim to address two issues in this manuscript: a) the role of Gai2 in neural crest development; and b) the mechanism of Gai2 function. While they have done a good job demonstrating a role of Gai2 in NC migration both in vivo and in vitro as well as the effects of Gai2 knockdown on cytoskeleton dynamics, protein distribution of selected polarity and focal adhesion molecules, and Rac1 activation, the link between Gai2 and the downstream effectors is largely correlative. Because of this, the model suggesting the sequential events flowing from Gai2 to microtubule to Rac1 to focal adhesion/actin should be modified to allow room for direct and indirect regulation at potentially multiple entry points.

Specific major comments are as the following:

Strengths:

-Determination of a role of Gai2 in neural crest migration is novel. -The effect of Gai2 knockdown on membrane protrusion morphology and microtubule stability and dynamics are demonstrated nicely. -Quantification of experimental perimeters has been performed throughout the manuscript in all the figures, and statistical analysis is included in the figures.

Weaknesses:

• The heavy focus of the study on microtubule is due to the previous publication on the function of Gai2 in regulation of microtubule during asymmetrical cell division. However, the activity of Gai2 is likely cell type-specific, as it has not been shown to control microtubule during cytokinesis in general. It is equally likely that Gai2 primarily regulates Rac1 or actin regulators to influence both microtubule and actin dynamics. The tone of the discussion should therefore be softened.
• The effect of rescue of NC migration with Rac1 inhibitor is marginal and the result is hard to interpret considering the inhibitor also blocks control NC migration. Either lower doses of Rac1 inhibitor can be used or the experiment can be removed from the manuscript, as Rac1 is required for membrane protrusions and the inhibitor doses can be hard to titrate.
• Since the defects seem to result partially from the inability of the NC cells to retract and move away, it may help to either include some data on Rho activation patterns in knockdown cells or simply add some discussion about the issue.
• To consider focal adhesion dynamics, live imaging should be used in the analysis. The fixed samples are different from each other, and natural variations of focal adhesion may exist among the samples. This can obscure data collection and quantification.

Minor comments

• Fig. 2, the centrosomes in control cells are not always obvious. The microtubules simply seem to be more networked and more fluid in control cells. This should be clarified with either marking the centrosomes in the figure or modifying the wording in the manuscript.
• In Fig. 3, a better negative control for co-IP should be using anti-V5 antibody to IP against tubulin/EB1/EB3 in the absence of Gai2-V5.
• The data for cell polarity proteins Par3 and PKC-zeta seem to be out of place. It is unclear whether mis-localization of these proteins has anything to do with NC migration defects induced by Gai2 knockdown. The conclusion does not seem to be affected if the data are taken out of the manuscript.
• In Suppl. Fig. 1, protrusion versus retraction should be defined more clearly. The retraction shown in this figure seems to be just membrane between protrusions instead of actively retracting membrane.
• Discussion can be improved by better incorporating all the components to make a cohesive story on how Gai2 works to regulate migration in the context of the neural crest cells.

Referees cross-commenting I agree with other reviewers' comments.

Significance

The authors demonstrate a role of Gai2 in regulation of neural crest migration in Xenopus by modulating microtubule dynamics. In addition, they show an effect of Gai2 knockdown on Rac1 spatial activation and focal adhesion stability. These are novel discoveries of the study. Some limitations exist in linking Gai2 with downstream effectors that directly or indirectly impact on cytoskeleton and Rac1 small GTPase.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This manuscript examines the role of a G protein, Gai2, in regulating the migration of cranial neural crest cells. Although previous literature has established that heterotrimeric G proteins are involved in cell migration, a central process during embryogenesis and adult homeostasis, the underlying cell biological mechanisms of their activities have not been elucidated. This manuscript rigorously examines the various aspects of Gai2 protein interactions to generate an exciting new paradigm in which Gai2 maintains normal microtubule dynamics by binding to tubulin and EB proteins. This normally dynamic microtubular intracellular environment then promotes cortical actin formation in the leading edge of the migrating cell as well as rapid focal adhesion disassembly by controlling Rac1 activity. Under conditions in which the levels of Gai2 are reduced by MO-mediated knockdown, cells display reduced microtubule dynamics and a decreased catastrophe rate, resulting in slower and more stable microtubules to which EB3 is more persistently associated. A stable microtubule environment leads to enhanced Rac1 activation at the leading edge and stable and larger focal adhesions, resulting in reduced migration. The authors utilize cutting edge approaches to examine the interactions between Gai2 and these other cellular components, taking advantage of the well characterized cell migration model - the cranial neural crest - both in embryos and in cultured explants of these cells.

Major comments:

The manuscript is mostly well written (it could use a few minor grammatical corrections), the significance of the problem is well described, and the results are clearly presented with adequate controls. The movies, provided as supplementary material, are of the highest quality and are essential additions to the stills provided in the figures. The data convincingly support the key conclusions of the manuscript.

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? No additional experiments are essential.

Are the experiments adequately replicated and statistical analysis adequate? The number of embryos/ explants per assay and the number of explant replicates for each assay and the statistical assessments are rigorous.

Are the data and the methods presented in such a way that they can be reproduced? Mostly, however, the description of the MO used for Gai2 knockdown needs more detail:

1. Does the MO knockdown both S and L homoeologs of X. laevis? Since the level of GAPDH in Figure 1H also looks reduced in Gai2 MO lane, it should be made clear that the apparent knockdown of Gai2 was normalized to GAPDH, rather than being the results of unequal loading of the gel. Yes, I recognize that Figure 1I says normalized, but this is not stated in the results or the methods. Also, was this experiment done with X. laevis or X. tropicalis? I could imagine that if done in X. laevis, the lack of complete knockdown might be due to only one homoeolog being affected.
2. The knowledge of the efficacy of knockdown in each Xenopus species provided by the information requested in the previous point, would allow the reader to assess the level of knockdown in the remaining assays. To do this, the authors should tell us which assays were done in which species. I am not suggesting that each experiment needs to be done in each species, only that the information should be provided. If the MO is more effective in X. tropicalis - which assays used this species? If the knock down is partial, as shown in Figure 1H-I, which species this represents in the remaining assays would be useful knowledge.

Minor comments:

While prior studies are referenced appropriately, and the text and figures are mostly clear and accurately presented, the following are a few suggestions that would help the authors improve the presentation of their data and conclusions:

1. The cell biological experiments convincingly demonstrate that knockdown of Gai2 causes cells to move more slowly. It would be a nice addition to bring the explant experimental data back to the embryo by showing whether the slower moving NC cells in morphants eventually populate the BA. DO they cease to migrate or are they just slower getting to their destination? This could be done by performing snail2 ISH at a later stage (34-35?)
2. There are places in the manuscript where the authors use the terms "silencing" or "suppression" of Gai2, when they really mean reduced translation - their system is not a genetic knockout, as clearly demonstrated in Figure 1H-I. I suggest that more accurate wording be used.
3. In Figures 1-5 there are scale of bars on the cell images, but these are not defined in any of the figure legends.
4. The abstract is the weakest section of the manuscript, and would have greater impact if it were more clearly written.

Referees cross-commenting

The concerns are fair assessments. However, most can be addressed in the text and by clearer presentation of existing data rather than more experimentation.

Significance

The molecular regulation of cell movement is a key feature of a number of developmental and homeostatic processes. While many of the proteins involved have been identified, how they interact to provide motility has not been elucidated in any great detail, particularly in embryo-derived cells (as opposed to cell lines). The results obtained from the presented experiments are novel, in-depth and provide a novel paradigm for how G proteins regulate microtubule dynamics which in turn regulate other components of the cytoskeleton required for cell movement. The results will be applicable to many migrating cell types, not just neural crest cells.

Because of the application of the data to many types of cells that migrate, the audience is expected to include a broad array of developmental biologists, basic cell biologists and those interested in clinically relevant aberrant cell migrations.

Reviewer keywords: Xenopus embryology; neural crest gene expression; use of MO-mediated knockdown of gene expression. Not an expert in microtubule dynamics.

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Reply to the reviewers

We are very grateful to the reviewers for their positive appraisal of the manuscript and for their useful comments and suggestions. Below are our answers and corresponding modifications of the manuscript.

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Reviewer #1

1 - Figures 1&4 focus on JU1264 as the primary double-sensitive strain. However, the authors built their RILs with HK104 by crossing with JU1498 in Figures 7&8. In the results section and/or methods, the authors should provide some justification for this strain switch. Alternatively, the equivalent analysis of Figure 1 focusing on JU1498 would be valuable to demonstrate that the effects of both viruses on fitness are similar to JU1264. I am not recommending that the JU1264xHK104 crosses be performed or that Figures 7&8 be repeated with JU1264xHK104 lines, but that more explanation for strain selection for RIL generation should be provided.

JU1264 and JU1498 are the strains where SANTV and LEBV were found, respectively. The experiments were performed over the years by different authors and were designed to answer different questions. JU1264 was the strain where the first virus was found and was used as a doubly sensitive strain in Figure 1 and the small RNA experiment. The main reason we chose JU1498 for genetic crosses to discover the genetic basis of LEBV sensitivity is that LEBV was detected and isolated from JU1498. Note that the JU1264 and JU1498 strains come from France and are in the same isotype group at CaeNDR (see also Figure 3) so the two strains may be interchangeable (although we cannot be sure).

We added in the text concerning the RIL construction: "We chose to use JU1498 as the LEBV-sensitive strain as it was the original strain in which LEBV was discovered."

2-The authors reasonably claim that the resistance of tropical strains like AF16 could be due to blocking viral entry or early inhibition of replication before the small RNA response is activated. Could the authors test this by directly microinjecting virus (in combination with a dye as a control for successful injection) into the intestine? I understand this could not be done on a scale that would allow for small RNA sequencing, but one could perform small-scale FISH to determine if LEBV or SANTV are replication-competent if the entry barrier is artificially overcome. Such an experiment may require considerable technical development. It may be beyond the scope/timing of this specific study, but it is worth considering to gain some insight into the possible resistance mechanisms observed.

Although the suggested experiment is in principle a great approach, it is difficult to perform without losing animals during the FISH staining. In addition, in this manuscript we are not particularly searching for the resistance mechanisms of AF16 but trying to present a wider perspective concerning viral infections of C. briggsae and their specificity. We performed small RNA analysis for AF16 together with the sensitive strains and therefore we commented on the lack of small RNA response in AF16 comparing to the sensitive strains. We thus consider that setting up intestinal injections at this point is arduous and beyond the scope of this manuscript.

Minor Comments: Line 78 - provide the full genus name for Caenorhabditis elegans at first appearance, as done for Caenorhabditis briggsae

This was modified. Line 117 - The description of cul-6 could also reference Bakowski et al. 2014. This study is referenced more generally as a player in proteostasis a few lines below but could be more explicitly tied to cul-6-mediated resistance to ORV (Bakowski et al. 2014 - see Fig. 7A) This section focus on the use of natural polymorphisms but we added this reference, which is indeed key for the effect of cul-6 knockdown on viral infection in C. elegans. Line 197-198 - The authors could consider adding sequences for FISH probes as part of Table S2. This information could add value to the present study even if previously listed in Frézal et al. We actually removed them from an earlier version since these sequences are already published: here and in further work, it seems preferable to refer to the primary study where these probes were designed, Line 263 - Were embryos obtained by bleaching of gravid adults, or was an egg lay performed, and the embryos were collected from plates? This is potentially an important distinction and should be clarified briefly in the methods. In the section “Preparation of small RNA libraries”, we obtained embryos by bleaching gravid adults.

We changed the first sentence to “Gravid hermaphrodites from uninfected cultures (AF16, HK104 and JU1264) were harvested using M9 solution, then bleached and washed twice using nuclease-free water. Embryo concentrations were estimated by counting embryos under the dissecting microscope and diluted to 2 embryos per mL of nuclease-free water. 200 embryos of each strain (AF16, HK104 and JU1264) were then plated onto 55 mm NGM plates seeded with E. coli OP50.” We also added “The embryos were obtained by bleaching gravid hermaphrodites.” to the Figure S5 legend. Line 330 - Provide justification for using JU1498 to make these RILs (see comment above). We added this sentence in the Results section. "We chose to use JU1498 as the LEBV-sensitive strain as it was the original strain in which LEBV was discovered." Line 446-Refer to the methods section for full clarity on the role of FISH in this set of experiments or reword for improved clarity. At first read-through, this phrasing made me expect some FISH experiments associated with Fig. 1, which does not appear to be the case.

We did perform FISH experiments as control that the cultures were infected, as explained in the Methods. We removed this mention from the Results section. Line 478 - The supplementary figure callouts are misaligned with the provided documents. S2A in the text appears to refer to S3A RT-qPCR results. Changed. Line 483 - Similar to above, the text suggests serial dilutions should refer to S4, not S3. Changed. Line 498 - Modify the text to 'Figure 2C and Figure 3' for clarity. Changed. Line 531,535 - viRNAs are defined in line 535 but this should be moved to 531 above at first appearance in the text. Changed. Line 593 - Typo in 'Logarithm of Odds?' Corrected. Line 621-624 - I recommend the authors include the data for the LEBV control experiments with NIL strains, either as a supplementary table, an additional panel for Fig. 6, or represented as done in Figure 8. We removed this sentence. Line 625-632 - How many total genes are represented in the QTL on IV? The reasoning behind testing rde-11 and rsd-2 is sound, but readers might want to know other potential candidates within this region (perhaps something the authors could also speculate on in the discussion). A similar comment applies for # genes in the QTLs on II and III.

We added in Table S7 the list of detected SNPs and short indels in the chromosome IV region and now indicate in the text "among them over 2700 SNPs and short indels (Table S7)." We added Table S11 with the polymorphisms in the chromosome II QTL region. We note that these tables do not include possible structural variants. The chromosome III QTL being weak, we abstained for this one but the data can now be found using CaeNDR.

Line 991-992 - Figure 1B - LEBV, SANTV, and co-infection effects on body size are mentioned but not quantified. Has this phenotype been quantified elsewhere? If so, the authors should reference it in the results section or Fig. 1 legend. Alternatively, body size could be quantified as part of this study and added to Fig. 1.

Because we do not have a large amount of data on body size, we removed "Body size quantification” from Figure 1B legend. Line 1001 - There is a typo in the first sentence; the period after LEBV should be removed. Small suggestion: Figure 2A - While described in the methods, I recommend that the authors briefly reiterate in the figure legend that the white/yellow boxes are intended to indicate serial chunking for clarity.

We removed the typo and explained the agar chunk representation in the figure legend: "The transfer by chunking a piece of agar is indicated by beige rectangles cut out from one plate and transferred to the next plate." Line 1034 - Small formatting note for Figure 4B - percentages of reads mapping to RNA1 and RNA2 appear underneath gridlines for the graph which obscures visibility and is inconsistent with the other graphs presented.

This was modified and is indeed clearer. Line 1094 - Figure S1 - this analysis could be strengthened by RT-qPCR represented as fold change in viral load instead of, or in addition to, the agarose gel image (like Fig. S3). Doing so would also allow for the normalization of eft-2 control across individual samples (e.g.: particularly low eft-2 amplification in ED3073). However, these results are sufficiently convincing that LEBV does not replicate in C. elegans, but a more quantitative approach is recommended if feasible for the authors. Alternatively, an additional figure panel and/or repeat of this analysis with C. elegans infected with ORV would also be beneficial as an additional control.

We do not understand how we can estimate a viral load by a ratio when we do not seem to see any significant amplification. Of course, a RT-qPCR would provide a finite Ct value and a ratio but they are likely to be meaningless. The ED3073 sample did not amplify for eft-2 either and calculating a ratio of high Ct values in a RT-qPCR would be misleading. We could remove the two ED3073 lanes but prefer to leave them.

Line 1112 - "Experiments using RNA2 primers gave similar results" - if this data isn't included in the study, this text should be removed.

Removed. Line 1141 - Figure S6 - For full transparency, the authors could consider including HK104 infected with LEBV to show minimal (zero) reads align to the RNA1/RNA2 segments using scales consistent with JU1264 infected with LEBV (S6C) The proportion of reads mapping (0%) are provided in Figure 4A and supplementary tables. We do not show the distribution of antisense 22G and sense 23nt along the LEBV genome for the HK104 (co)infections for the following reasons. 0% of these reads map to LEBV in HK104 monoinfection, and only 0.02% antisense 22G in coinfection. Moreover, the 23nt reads mapping to LEBV-RNA2 in the HK104 coinfection (16.54%;1931 reads) correspond to a 41 bp region with 85% nucleotide similarity between SANTV-RNA2 and LEBV-RNA2. Overall, the few 23nt (+) reads mapping to LEBV in HK104 coinfection are most likely a spillover of the HK104 antiviral response to JUv1264 entry into the intestinal cells.

Reviewer #2

Main points: 1. In figure 1C and D, is more than 1 biological replicate performed? Ideally multiple independent infections would be performed which would increase confidence in these experiments, but minimally the authors should make clear that this data was from an experiment only performed once. The conclusion from the life span assays is unlikely to change, but given the variance of the brood size assays within replicates, the conclusions that LEBV infection reduces the brood size is weakly supported.

We added “Panels C-D correspond to a single experiment (see Methods).” to the legend of Figure 1. We changed the wording to "LEBV and especially the co-infection appeared to lower brood size." We do not have data for independent experiments.

If the authors want to claim that there is a defect in viral entry in the resistant strains, they should perform infections experiments at an earlier time point that could capture viral invasion. In C. elegans with Orsay virus these experiments have been done as early as 18 hours by FISH. https://journals.plos.org/plospathogens/article?id=10.1371/journal.ppat.1011120 The way the assays are currently set up, if the infection was cleared it wouldn't be observed.

The strongest point that indicates that the virus does not replicate is the small RNA experiment, in which the animals were collected on the initial plate inoculated with the virus. We think that our wording was careful:

We further amended it:

• in Results " The animals were collected for sRNA sequencing on the plates onto which the viral inoculate was added and where they were constantly exposed to the virus".

• in Discussion " Indeed, as we did not assay viral entry by sensitive FISH or RT-PCR at early timepoints, it is possible that the viruses are cleared without production of small RNAs."

The evidence that the region on chromosome III contributes to susceptibility is weak. The analysis in figure 5B does not identify this region and it is not clear to me how to read the scale in figure 5C to determine that a region on chromosome III is significant.

We added in the Figure legend: "with a LOD score of 10.5, above the threshold calculated by simulations (see Methods)." and detailed the method in the Methods section (see reply to Reviewer 3 below).

In figure 6 using a more appropriate statistical test such as one way ANOVA with multiple hypothesis testing is necessary to determine if there is a difference between JU2832 and JU2916. It would be helpful if the authors could add more discussion of the evidence that they feel that supports this region being involved in susceptibility.

We do not think that an ANOVA is appropriate to analyze these proportions which cannot have normal distributions of residuals, therefore we used a generalized linear model, taking genotype and block (day of experiment) into account. This was only explained in the legend and is now explained in the Methods section as well. Maybe the reviewer suggests us to us a global analysis with strain as a factor. We could do this but we do not think that it applies well to this situation: here we test for a specific hypothesis for each one-QTL strain. We have corrected for multiple testing as explained next. The legend now reads: " The significance p values were obtained in a generalized linear model (glm) taking independent experimental blocks and infection replicates into account, testing NILs against their relevant background parent. The p values using the two strains testing for the QTL on chromosome IV and those using the two-QTL strain JU2832 are corrected for multiple testing." In addition, we now provide p values rather than three stars, which reinforce the point (they are very low).

Minor points 1. In figure 1B it would be helpful to provide more information on the animals chosen to display. Are these representative examples or extreme examples?

These are representative examples. This detail was added in the legend.

In figure 2B, adding a legend for the colored dots would be helpful.

We had indicated: "Dots are replicates within a block, with 100 animals scored per replicate (see Table S4 for the detailed results and Figure S2 and Methods for the experimental design). Experimental blocks are represented by colors and the bar indicates the grand mean of the blocks." 3. In figure 2C, the definitions for a strain to be labeled as belonging to each category should be provided.

The categorization method is now explained in the Methods section. In addition, Figure 2C legend now refers to Table S4 for the category of each strain. 4. Could the data in figure 2 be used for genome-wide association mapping and compared to the RIL QTL experiments? Adding comment on this would be helpful to understanding the usefulness of this data.

There are too few strains here to test genome-wide for association. If we had the causative SNP, it would be interesting to assess its frequency but this is beyond the focus and scope of this work, which focused on the outlier phenotype of the HK104 strain. 5. In figure 4b, in HK104 LRBV the numbers in top right corner are not defined.

We added to the legend of Figure 4B: “For the HK104 infection with LEBV, the number of read counts is provided in the top right corner to signal their rarity compared to ca. 107 in the other conditions. See Table S5 for all read counts. ” 6. Line 1001 remove period from "LEBV.of" and add period after isolates. Removed.

Reviewer #3 Major comments • The authors provide most data in both a processed and raw format, which is helpful. In two cases (data from 3 DPI, line 492 and LEBV infections in the AF16xHK104 NILs, line 621), the authors state their results, but the data seems not to be provided in the document (at least no direct reference is provided). These are supporting results and do not affect the main conclusions, nevertheless providing the data in form of a table or supplementary figure would be required. Generally, it may help to include a data availability statement to have a combined overview of where data can be found.

As noted by the reviewer, we tried to provide the data in raw format, but did not judge it necessary when the experiment had two datapoints that are provided in the text. We added the number of animals in the instance where it was missing.

Minor comments • Line 97-126: Here the manuscript fully focuses on the work in C. elegans. It would be interesting to make clear links to the work in C. briggsae (e.g. mention if homologs are present). The paragraph in line 127 clarifies advantages of studying viral infection in C. briggsae compared to C. elegans. It may be logical to place this information early in the text.

We added a sentence to link the C. elegans work and C. briggsae. • Line 166 and results from this experiment: Is the LEBV-SANTV mixture consisting of 50uL of both viruses or a total of 50uL (so 25uL of both)? This is also important for the interpretation of results.

To clarify, we changed to: “50 l ... of an equivolume mix of SANTV and LEBV”. • Line 167: The text says the culture is maintain for 4 days, but then also mentions day 5. Figure 2 clarifies the experimental setup later, but the text could be clearer here.

Thank you for noticing this. We changed the 4 to 7. • Line 172: What are the nine starter cultures?

The nine starting cultures were those obtained as described in the paragraph preceding this line in the manuscript. From a plate of infected animals (five L4 larvae), we propagated the infected population by chunking over 3 plates (day 3) and 3*3 plates (day 5). To make this point clear, we have added above: "to generate for the following experiments nine starter cultures for each of the four conditions " • Line 185: 'Infection of the set of C. briggsae natural isolates'. From the text it is not clear what set the authors refer to.

We changed to "a set" and refer to Figure 2B and Table S4 in the sentence below for the list of natural isolates. • Line 223: 'The proportion of infected animals were overall higher in Batch3 but the qualitative results are similar'. It is unclear why this statement is here instead of in the result section and it is also not clear what the authors mean by the second part of the sentence.

We moved the sentence to Results and changed it to: " The proportion of infected animals were overall higher in Batch 3 but the relative results of the different strains were similar for the three batches." • Line 326: Is 'the same method as above' using FISH or RT-qPCR?

Changed to "using FISH as above". • Line 382: What do the authors mean by 'two cross directions'?

We removed this mention as the method is better explained in the next sentence.

• Line 454-458: The data presented here does not appear well integrated in the storyline. It does not fit under the subheading. Perhaps it would be a better fit under the subheading of line 462? We moved it below the subheading. • Line 478: Reference to Fig S2 should be reference to Fig S3

Changed. • Line 483: Reference to Fig S3 should be reference to Fig S4

Changed. • Line 540-544: The sentence reads as a contradiction (C. elegans defends itself using RNAi, C. briggsae blocks viral infection during entry). As a result, the sentence reads as if RNAi is not of much antiviral importance in C. briggsae, but that cannot be concluded from this data. I am not sure if this is what the authors aim to suggest, but another word choice (e.g. changing 'whereas' and 'this does not seem the case for C. briggsae') may be considered.

We changed the wording to " whereas the C. elegans N2 reference strain allows for viral entry and defends itself against ORV via its small RNA response (Félix et al. 2011; Ashe et al. 2013; Shirayama et al. 2014; Coffman et al. 2017), in the tested resistant C. briggsae strains, the viruses appeared to be blocked at entry or at early steps of the viral cycle." • Line 585 and 592: There are two QTL approaches being applied and referred to as 'the one- and two-QTL analyses'. The description in this part is rather technical and the terminology is not clear. As a result, for readers not familiar with QTL mapping, the biological interpretation may become obscured.

We now explain in Methods: " ...scanning each pair of positions for several models, including single-QTL, full, additive and epistatic. The significance threshold LOD score of each model was estimated via 1,000 permutation tests with a coefficient of risk a=0.05. The threshold was 4.91 for the additive model and 6.09 for the full model. The LOD score of each pair of position is represented by a color scale in Figure 5C). The combination of the chromosomes III and IV QTLs had a LOD score of 10.5 in the full and additive models. No epistatic interaction was detected. The LOD score of the single-QTL model comparison was below the threshold."

• Line 659: The authors end the section about natural genetic variation in the response to SANTV with candidate genes and a CRISPR experiment. As the authors identify a small genetic region associated with LEBV susceptibility, it would be interesting to hear about any candidate genes in this region. There are still many genes and more importantly, many polymorphisms in this region (ca. 700 single-nucleotide polymorphisms and short indels). Because structural variants are difficult to call (long-read sequencing has not been performed on the parents), we had preferred to abstain to provide a list of polymorphisms that would be incomplete and preferentially point towards SNPs. However, because of the reviewer's query, we now provide it in Table S11.

• Line 674: The authors make use of HK104 strain in this study as it is the exception in their dataset that provides resistance against LEBV, but not SANTV. Possibly, the genetic variation linked to viral susceptibility uncovered using HK104 may therefore be relatively uncommon in C. briggsae. The implications of this choice and option for other studies using different genotypes could be interesting to discuss in this short paragraph. The aim in here is to discover why HK104 is specifically resistant to one virus and not the other. There is a possibility of uncovering a specific mechanism that is present in only two or three strains of our 40-strain dataset but we find this specificity particularly

interesting, regardless of its prevalence. We explore in the Discussion which of the two crosses may reveal the specificity.

• Line 774: The IPR is already described on abbreviated in line 742. As a reader, we prefer having the abbreviation explained twice than not understanding it. • Overall, to reach a broader audience, the manuscript can expand explanations in the discussion. E.g. statements in line 695 and 773, refer to previous observations, but do not explain them in enough detail to understand parallels between this and previous studies without prior knowledge.

We added some explanations, specifically for lines 695 and 773 (of previous version). • Figure 2: Only HK104 is labelled in the figure, it would be useful to also see HK105 as this strain is also explicitly mentioned in the text.

We now included HK105 and strains that are used in further experiments.

• Figure 2: It is not clear from the results or methods how strains as designated into a certain class. The figure legend says variability in the data is taken into account and that is why some strains are close to each other, yet distinct in class, but how this works is not described. We now explain our criteria. See above in the response to Reviewer 2. • Figure S3: The strain JU1264 and JU1498 are mentioned thrice (as '2', 'rep' and 'ref'). These annotations should be clarified.

These explanations were indeed missing. We now explain them in the figure legend. • Figure S4: The figure would benefit from a division in panels per strain to facilitate comparisons across strains.

Indeed. We now added a division in panels per strain. • Figure S4: Have the authors correlated viral loads with the number of infected animals? This could result in addition information if not all individuals are infected equally.

We have not done so in this precise experiment but preferred to use the number of infected animals in most other experiments, in particular because it is less subject to outlier effects. • Figure S4: Could the authors clarify the meaning of JU1264 Rep?

It is explained in the legend: "The undiluted viral preparations on JU1264 are used to normalize and are indicated as "JU1264 1/1". A separate replicate was performed and indicated as "JU1264 Rep"."

• Figure 8: The meaning of the stars in this figure is a bit confusing and the description of these stars in the legend is not clear. Indeed. We changed the legend to: " ***: p<0.001 comparing JU4034 with its parent strain HK104 using a generalized linear model."

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Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript provides new and detailed insight into two viruses infecting Caenorhabditis briggsae, a close relative of the widely studied model organism Caenorhabditis elegans. The authors study infection from a host perspective using two out of three viruses known to infect C. briggsae. The study mostly focuses on unravelling genetic variation within the host that links to viral susceptibility. They identify and confirm three QTL locations. They subsequently create CRISPR mutations to study candidate genes. Moreover, the study provides novel molecular insight into the C. briggsae antiviral RNAi pathway. Overall, the study provides a good basis to continue using C. briggsae to study viral infection.

Major comments

• The authors provide most data in both a processed and raw format, which is helpful. In two cases (data from 3 DPI, line 492 and LEBV infections in the AF16xHK104 NILs, line 621), the authors state their results, but the data seems not to be provided in the document (at least no direct reference is provided). These are supporting results and do not affect the main conclusions, nevertheless providing the data in form of a table or supplementary figure would be required. Generally, it may help to include a data availability statement to have a combined overview of where data can be found.

Minor comments

• Line 97-126: Here the manuscript fully focuses on the work in C. elegans. It would be interesting to make clear links to the work in C. briggsae (e.g. mention if homologs are present). The paragraph in line 127 clarifies advantages of studying viral infection in C. briggsae compared to C. elegans. It may be logical to place this information early in the text.
• Line 166 and results from this experiment: Is the LEBV-SANTV mixture consisting of 50uL of both viruses or a total of 50uL (so 25uL of both)? This is also important for the interpretation of results.
• Line 167: The text says the culture is maintain for 4 days, but then also mentions day 5. Figure 2 clarifies the experimental setup later, but the text could be clearer here.
• Line 172: What are the nine starter cultures?
• Line 185: 'Infection of the set of C. briggsae natural isolates'. From the text it is not clear what set the authors refer to.
• Line 223: 'The proportion of infected animals were overall higher in Batch 3 but the qualitative results are similar'. It is unclear why this statement is here instead of in the result section and it is also not clear what the authors mean by the second part of the sentence.
• Line 326: Is 'the same method as above' using FISH or RT-qPCR?
• Line 382: What do the authors mean by 'two cross directions'?
• Line 454-458: The data presented here does not appear well integrated in the storyline. It does not fit under the subheading. Perhaps it would be a better fit under the subheading of line 462?
• Line 478: Reference to Fig S2 should be reference to Fig S3
• Line 483: Reference to Fig S3 should be reference to Fig S4
• Line 540-544: The sentence reads as a contradiction (C. elegans defends itself using RNAi, C. briggsae blocks viral infection during entry). As a result, the sentence reads as if RNAi is not of much antiviral importance in C. briggsae, but that cannot be concluded from this data. I am not sure if this is what the authors aim to suggest, but another word choice (e.g. changing 'whereas' and 'this does not seem the case for C. briggsae') may be considered.
• Line 585 and 592: There are two QTL approaches being applied and referred to as 'the one- and two-QTL analyses'. The description in this part is rather technical and the terminology is not clear. As a result, for readers not familiar with QTL mapping, the biological interpretation may become obscured.
• Line 659: The authors end the section about natural genetic variation in the response to SANTV with candidate genes and a CRISPR experiment. As the authors identify a small genetic region associated with LEBV susceptibility, it would be interesting to hear about any candidate genes in this region.
• Line 674: The authors make use of HK104 strain in this study as it is the exception in their dataset that provides resistance against LEBV, but not SANTV. Possibly, the genetic variation linked to viral susceptibility uncovered using HK104 may therefore be relatively uncommon in C. briggsae. The implications of this choice and option for other studies using different genotypes could be interesting to discuss in this short paragraph.
• Line 774: The IPR is already described on abbreviated in line 742.
• Overall, to reach a broader audience, the manuscript can expand explanations in the discussion. E.g. statements in line 695 and 773, refer to previous observations, but do not explain them in enough detail to understand parallels between this and previous studies without prior knowledge.
• Figure 2: Only HK104 is labelled in the figure, it would be useful to also see HK105 as this strain is also explicitly mentioned in the text.
• Figure 2: It is not clear from the results or methods how strains as designated into a certain class. The figure legend says variability in the data is taken into account and that is why some strains are close to each other, yet distinct in class, but how this works is not described.
• Figure S3: The strain JU1264 and JU1498 are mentioned thrice (as '2', 'rep' and 'ref'). These annotations should be clarified.
• Figure S4: The figure would benefit from a division in panels per strain to facilitate comparisons across strains.
• Figure S4: Have the authors correlated viral loads with the number of infected animals? This could result in addition information if not all individuals are infected equally.
• Figure S4: Could the authors clarify the meaning of JU1264 Rep?
• Figure 8: The meaning of the stars in this figure is a bit confusing and the description of these stars in the legend is not clear.

Significance

The study contains a large amount of experimental data that provides a solid basis for using C. briggsae as a model to study viral (co-)infections. Interesting comparisons to C. elegans that is more thoroughly studied are drawn and used to advance understanding of viral infection for both organisms. Diverse experimental approaches have been taken to support conclusions and the data is thoughtfully considered throughout the manuscript. Sometimes, the text or presentation of the figures could be improved for clarity. The current manuscript will be of most interest for an audience with some knowledge about viral infections in nematodes and/or an interest in natural genetic variation or RNAi in C. elegans. Moreover, further development of model organisms like the Caenorhabditis nematodes for study of viral infection is of broad interest to virologists.

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Referee #2

Evidence, reproducibility and clarity

Viruses are common parasites of most animals and hosts have evolved a variety of mechanisms to defend against viruses. C. elegans and its natural Orsay virus have been used to discover novel mechanisms of viral immunity. Understanding the genetic basis why some hosts get infected and others do not can lead to a better mechanistic understanding of viral infection. In this manuscript, the authors describe their characterization of strain-specific differences in immunity to Santeuil and Le Blanc viruses in their natural nematode host C. briggsae. They found that particular strains of C. briggsae were sensitive or resistant to either or both viruses corresponding to the geographic origins of the strains. Resistant strains were determined to lack a small RNA response to infection suggesting an alternate, pre-invasion method of resistance. QTLs corresponding to resistance in both viruses were identified through utilization of Advanced Intercrossed Recombinant Inbred Lines (RILs).

Main points:

1. In figure 1C and D, is more than 1 biological replicate performed? Ideally multiple independent infections would be performed which would increase confidence in these experiments, but minimally the authors should make clear that this data was from an experiment only performed once. The conclusion from the life span assays is unlikely to change, but given the variance of the brood size assays within replicates, the conclusions that LEBV infection reduces the brood size is weakly supported.
2. If the authors want to claim that there is a defect in viral entry in the resistant strains, they should perform infections experiments at an earlier time point that could capture viral invasion. In C. elegans with Orsay virus these experiments have been done as early as 18 hours by FISH. https://journals.plos.org/plospathogens/article?id=10.1371/journal.ppat.1011120 The way the assays are currently set up, if the infection was cleared it wouldn't be observed.
3. The evidence that the region on chromosome III contributes to susceptibility is weak. The analysis in figure 5B does not identify this region and it is not clear to me how to read the scale in figure 5C to determine that a region on chromosome III is significant. In figure 6 using a more appropriate statistical test such as one way ANOVA with multiple hypothesis testing is necessary to determine if there is a difference between JU2832 and JU2916. It would be helpful if the authors could add more discussion of the evidence that they feel that supports this region being involved in susceptibility.

Minor points

1. In figure 1B it would be helpful to provide more information on the animals chosen to display. Are these representative examples or extreme examples?
2. In figure 2B, adding a legend for the colored dots would be helpful.
3. In figure 2C, the definitions for a strain to be labeled as belonging to each category should be provided.
4. Could the data in figure 2 be used for genome-wide association mapping and compared to the RIL QTL experiments? Adding comment on this would be helpful to understanding the usefulness of this data.
5. In figure 4b, in HK104 LRBV the numbers in top right corner are not defined.
6. Line 1001 remove period from "LEBV.of" and add period after isolates.

Significance

Overall, this is an interesting and well-carried out study that describes a new system for understanding the genetic basis to viral infection. Using C. briggsae as a comparative system to C. elegans is likely to gain further insight into the specificity of viral infections and if mechanisms of resistance are unique or shared between these two nematodes. This study is likely to be interesting to virologists, evolutionary biologists, and those studying host-pathogen interactions.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Alkan et al. investigate natural variation in the susceptibility of C. briggsae nematodes to two naturally occurring Noda-like RNA viruses, the Le Blanc (LEBV) and Santeuil (SANTV). Compared to the related nematode species, C. elegans, considerably less attention has been paid to immunity to viral infections, or causative genes, in other nematode species. Taking advantage of a large, globally distributed set of C. briggsae natural isolates, the authors infected these strains with LEBV, SANTV, or both viruses to comprehensively analyze natural variation in viral susceptibility. They generally find that strains isolated from temperate regions are sensitive to both viruses, while tropical strains are resistant. However, excitingly, they identify several strains (focusing specifically on HK104 from Japan) with virus-specific susceptibility. Using this observation, the authors rigorously investigate a suite of existing RILs and generate their own RILs/NILs to identify QTLs of chromosomes II, III, and IV with likely roles in LEBV and SANTV resistance. The authors could not narrow these QTLs to causative alleles in specific genes, but this work sets up future studies to further elucidate molecular mechanisms of resistance.

Additionally, the authors identify an interesting distinction between C. briggsae strains that are resistant to viruses compared to the more commonly studied C. elegans and its natural pathogen, the Orsay virus. Alkan et al. employ small RNA sequencing to demonstrate that LEBV and SANTV-resistant strains do not elicit a small RNA response. This suggests immunity occurs by blocking viral entry or early replication steps that precede RNAi induction. This contrasts with some C. elegans strains resistant to Orsay virus, like the N2 strain, in which a small RNA response is detected. Such a result highlights the value of investigating immune responses across distinct nematode species, as there are clearly different resistance mechanisms at play. Future work building on this study will further demonstrate the value of C. briggsae and other nematodes as valuable comparative models with C. elegans.

Major Comments:

Overall, I found this study's data convincing, statistically rigorous and well-executed. The author's conclusions are largely fair and supported by the presented data. I appreciated that the authors performed infection screens across multiple independently generated virus preps (a notoriously variable process) to increase confidence in the results. I have two suggestions that the authors should consider addressing before publication:

1. Figures 1&4 focus on JU1264 as the primary double-sensitive strain. However, the authors built their RILs with HK104 by crossing with JU1498 in Figures 7&8. In the results section and/or methods, the authors should provide some justification for this strain switch. Alternatively, the equivalent analysis of Figure 1 focusing on JU1498 would be valuable to demonstrate that the effects of both viruses on fitness are similar to JU1264. I am not recommending that the JU1264xHK104 crosses be performed or that Figures 7&8 be repeated with JU1264xHK104 lines, but that more explanation for strain selection for RIL generation should be provided.
2. The authors reasonably claim that the resistance of tropical strains like AF16 could be due to blocking viral entry or early inhibition of replication before the small RNA response is activated. Could the authors test this by directly microinjecting virus (in combination with a dye as a control for successful injection) into the intestine? I understand this could not be done on a scale that would allow for small RNA sequencing, but one could perform small-scale FISH to determine if LEBV or SANTV are replication-competent if the entry barrier is artificially overcome. Such an experiment may require considerable technical development. It may be beyond the scope/timing of this specific study, but it is worth considering to gain some insight into the possible resistance mechanisms observed.

Minor Comments:

Line 78 - provide the full genus name for Caenorhabditis elegans at first appearance, as done for Caenorhabditis briggsae

Line 117 - The description of cul-6 could also reference Bakowski et al. 2014. This study is referenced more generally as a player in proteostasis a few lines below but could be more explicitly tied to cul-6-mediated resistance to ORV (Bakowski et al. 2014 - see Fig. 7A)

Line 197-198 - The authors could consider adding sequences for FISH probes as part of Table S2. This information could add value to the present study even if previously listed in Frézal et al.

Line 263 - Were embryos obtained by bleaching of gravid adults, or was an egg lay performed, and the embryos were collected from plates? This is potentially an important distinction and should be clarified briefly in the methods.

Line 330 - Provide justification for using JU1498 to make these RILs (see comment above).

Line 446-Refer to the methods section for full clarity on the role of FISH in this set of experiments or reword for improved clarity. At first read-through, this phrasing made me expect some FISH experiments associated with Fig. 1, which does not appear to be the case.

Line 478 - The supplementary figure callouts are misaligned with the provided documents. S2A in the text appears to refer to S3A RT-qPCR results.

Line 483 - Similar to above, the text suggests serial dilutions should refer to S4, not S3.

Line 498 - Modify the text to 'Figure 2C and Figure 3' for clarity.

Line 531,535 - viRNAs are defined in line 535 but this should be moved to 531 above at first appearance in the text.

Line 593 - Typo in 'Logarithm of Odds?'

Line 621-624 - I recommend the authors include the data for the LEBV control experiments with NIL strains, either as a supplementary table, an additional panel for Fig. 6, or represented as done in Figure 8.

Line 625-632 - How many total genes are represented in the QTL on IV? The reasoning behind testing rde-11 and rsd-2 is sound, but readers might want to know other potential candidates within this region (perhaps something the authors could also speculate on in the discussion). A similar comment applies for # genes in the QTLs on II and III.

Line 991-992 - Figure 1B - LEBV, SANTV, and co-infection effects on body size are mentioned but not quantified. Has this phenotype been quantified elsewhere? If so, the authors should reference it in the results section or Fig. 1 legend. Alternatively, body size could be quantified as part of this study and added to Fig. 1.

Line 1001 - There is a typo in the first sentence; the period after LEBV should be removed. Small suggestion: Figure 2A - While described in the methods, I recommend that the authors briefly reiterate in the figure legend that the white/yellow boxes are intended to indicate serial chunking for clarity.

Line 1034 - Small formatting note for Figure 4B - percentages of reads mapping to RNA1 and RNA2 appear underneath gridlines for the graph which obscures visibility and is inconsistent with the other graphs presented.

Line 1094 - Figure S1 - this analysis could be strengthened by RT-qPCR represented as fold change in viral load instead of, or in addition to, the agarose gel image (like Fig. S3). Doing so would also allow for the normalization of eft-2 control across individual samples (e.g.: particularly low eft-2 amplification in ED3073). However, these results are sufficiently convincing that LEBV does not replicate in C. elegans, but a more quantitative approach is recommended if feasible for the authors. Alternatively, an additional figure panel and/or repeat of this analysis with C. elegans infected with ORV would also be beneficial as an additional control.

Line 1112 - "Experiments using RNA2 primers gave similar results" - if this data isn't included in the study, this text should be removed.

Line 1141 - Figure S6 - For full transparency, the authors could consider including HK104 infected with LEBV to show minimal (zero) reads align to the RNA1/RNA2 segments using scales consistent with JU1264 infected with LEBV (S6C)

Significance

C. elegans has received considerable attention as a model for host-natural pathogen interactions, including the Orsay virus, microsporidia species, oomycetes, and others. However, the field would benefit from increased diversification into related nematodes, as there is likely much more exciting biology to uncover beyond C. elegans. This study exemplifies the genetic advantages of nematodes for this purpose, given the diverse nematode strains available from the CaeNDR (Crombie et al. 2023, PMID: 37855690), rapid growth/genetics of nematodes, and ease of infection by naturally relevant pathogens. Anyone interested in innate immunity mechanisms to viruses or other intracellular pathogens will find this study valuable, as well as those generally interested in traits under selective pressures. My field of expertise is microsporidia as parasites of nematodes, which also act as intracellular pathogens of the intestine but are eukaryotic. Surprisingly, viruses and microsporidia overlap considerably in host immune response (Bakowski et al. 2014, Chen et al. 2017, Reddy et al. 2019 referenced in Alkan et al.). To date, this has been largely explored using C. elegans as a model, but microsporidia that infect C. elegans also infect C. briggsae (Wan et al. 2022 PMID:36534656, Wadi et al. 2023: 3741459). Thus, I view the work of Alkan et al. as opening the door to exciting new directions that could similarly be executed with microsporidia pathogens for comparative analysis in C. elegans, C. briggsae, and related nematodes.

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Reply to the reviewers

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

The manuscript by Xie et al investigates the role of efemp1 in mediating ocular growth. Efemp1, a secreted extracellular matrix glycoprotein, was previously identified as a myopia-risk gene in human GWAS studies. Given that myopia is linked to aberrant eye shape, the authors investigated whether and how this gene mediates eye growth. Using a CRISPR based approach in zebrafish the authors knocked out efemp1 specifically in the retina and established that a myopic eye results. They went further and investigated visual function in these mutant fish using the optomotor response and electroretinograms. As dark-rearing in many animal models has been linked to the induction of myopia, the authors examined the effects of a dark-rearing regimen in efemp1 mutants and found surprisingly that they did not show signs of myopia. Lastly, the expression and distribution of several myopia-associated genes was investigated in the retina of efemp1 mutants and following dark-rearing.

1. The starting point for this study was the generation of a "retina-specific knockout mutant of the efemp1 gene". However, evidence for a 'successful' knockout at the protein level is missing.

We have clarified the exact nature of our efemp12C-Cas9 model further. The mutants have mosaic genetic modification that do not simply lead to gene deletion (knockout). We have reworded throughout the manuscript to avoid statement indicating the efemp1 2C-Cas9 fish as a knockout model and instead used “genetic modification” or “genetic disruption”, etc:

“This gene editing system led to mosaic retinal mutations; each Cas9-expressing retinal cell that were driven by the rx2 promoter would perform its own CRISPR gene editing process, and as a result, even within an individual retina, there were different types of indels (e.g., loss- or gain-of-function mutations, or milder mutations that may cause mislocalization) in different cells.” (Line 104–108).

For the same reason, it is very challenging to show such a mosaic genetic editing in the protein level. First of all, we were not able to find commercial anti-EFEMP1 antibody for zebrafish that targets specifically the editing sites in our fish model. This means that mutated efemp1 DNAs that were transcribed and translated would produce mutant EFEMP1 protein that might still be recognized by an anti-EFEMP1 antibody, although their dysfunction might manifest as altered distribution and thus abnormal ocular development.

On the other hand, in this study we used a headloop PCR technique, a sensitive genotyping approach that specifically suppresses amplification of wild-type but not mutated efemp1 DNA to show that there were genetic modifications in our mutants. However, likely due to the patchy distribution of Cas9-expressing retinal cells (Fig 1A′) and the non-uniform nature of gene editing, our genotyping results showed weak mutant bands (Fig 1C–D), implicating low editing rates. The fact that only a proportion of mutations would result in loss of the protein would make it difficult to distinguish the gene editing in the retina via immunostaining or western blot.

We have added following in the Results section to indicate the difficulties in showing genetic modification at the protein level for the efemp12C-Cas9 model:

“On the other hand, due to the mosaic nature of the gene editing, the patchiness of Cas9-expressing retinal cells (Fig 1A′) and the potentially low editing rate, as well as the unavailability of commercial anti-EFEMP1 antibodies that targets specifically the CRISPR editing sites, efemp1 modification in our mutant model at the protein level is challenging to show.” (Line 125–128)

Immunostaining for Efemp1 in sections of the entire retina from control and mutant fish would have helped here. It is only in Figure 7 B, C that portions of the inner retina from control and efemp1 2c-Cas9 fish are shown with Efemp1 immunostaining. Control and mutant retinae show slight relative differences in Efemp1 fluorescence levels which are difficult to reconcile with a knock-out scenario.

As mentioned above, our model is not simply a knockout but a combination of a range of indels that may produce mutant proteins. At least some of them are therefore still likely to bind with the anti-EFEMP1 antibody used in the present study; the antibody does not bind to EFEMP1 regions corresponding to sgRNAs target sites on zebrafish efemp1 DNA. We have added this detail in the Methods to clarify.

“Noting that the anti-EFEMP1 antibody does not bind to EFEMP1 regions corresponding to sgRNAs target sites on zebrafish efemp1 DNA, thus mutant proteins (if any) may still be labeled by the antibody.” (Line 790–792)

Therefore, it makes sense that our result showed differences in relative EFEMP1 fluorescence between groups across the inner retina rather than complete loss of EFEMP1 immunostaining in mutant retinas.

resumably this phenotype is a result of the mosaic expression of Cas9 (GFP) shown in Fig 1? Can the authors explain the reason for this mosaicism?

We believe that the “mosaic expression of Cas9” the reviewer mentioned is the “patchy distribution of Cas9-expressing retinal cells” as we mentioned in the above response. Yes this is also partially the reason why mutant retinas still present EFEMP1 immunostaining. The patchy (or mosaic) Cas9 expression in the retina of our mutant model can be because we use the Gal4/UAS system to drive the 2C-Cas9 gene editing system. Mosaic expression has long been noticed as a drawback of the Gal4/UAS system. We have modified the manuscript to explain the mosaic Cas9 expression in the mutant retina:

“The patchiness of Cas9 expression in the mutant retina may attribute to the Gal4/UAS system (Halpern et al., 2008).” (Line 103–104)

Given this mosaic expression would one expect Efemp1 immunoreactive areas intermingled with areas devoid of Efemp1 in the mutant retina?

This happens only in cells that CRIPSR eliminates production of EFEMP1, but due to patchy Cas9 expression and perhaps only a little proportion of Cas9-positive cells will lose EFEMP1 protein, our immunostaining did not show apparent intermingling. Importantly, it is worth noting that as our explanation above, anti-EFEMP1 antibody may be able to bind with mutant EFEMP1 proteins and thus EFEMP1 immunostaining will still present in retinal cells with successful gene editing.

Further, do deficits in the various functional assays the authors perform correlate with the degree of mosaicism?

We appreciate the reviewer’s interesting idea. As primary goal of the present study is to determine whether retinal-specific efemp1 modification has any effect on ocular refraction, we aimed to use fish with as more Cas9-expressing cells as possible for functional analysis, and thus fish used were not expected to have discernible difference in degree of Cas9 expression mosaicism. Therefore, it is not known that whether there is a correlation between ocular deficits and Cas9 expression mosaicism. We thank the reviewer’s suggestion and will bear this idea in mind for future experimental design.

In the same vein, in Figure 2 the authors refer to variation in GFP levels in the efemp12c-Cas9. It is not clear whether the authors mean levels of GFP in individual cells or numbers of GFP+ cells. Presumably the latter. Could the authors clarify?

We have added details in the Methods of the manuscript to clarify:

“Post-hoc retinal histology indicated that intensity of eGFP fluorescence is corresponding to eGFP positive cell number; fish with higher eGFP fluorescence level had more eGFP positive cells.” (Line 723–725)

In my opinion understanding and characterizing the efemp12c-Cas9 fish thoroughly is key to interpreting the phenotypes the authors show subsequently.

We agree with the reviewer. Due to the characteristics of our 2C-Cas9 model mentioned above, headloop PCR, which is highly sensitive for determining occurrence of gene mutations regardless indel types, is so far the most practical approach for us to provide evidence of successful gene editing. Because there was limited means to show gene modification in the protein level for our mutant model (as mentioned above), we instead provided functional verification of gene modification using OMR. We showed that functionally our 2C-Cas9 model have comparable phenotype with efemp1-knockdown zebrafish that have robust gene disruption induced by morpholino. Overall, with this evidence we believe that there were efemp1 modification in our fish model. Given no other manipulations, the phenotypes are presumably due to the mosaic mutations generated here. We would speculate (though have no data to show this) that a more even and complete knockout of Efemp1 throughout all of the retinal neurons would increase the size of the phenotypic changes seen even more. It was important for us to target the eye to assess the role in the local emmetropisation processes rather than mixing it with possible other CNS defects confounding the phenotype. We were excited to be able to observe quantifiable phenotypes even with such a mosaic randomized mutation model shown here and believe it gives more strength to the role of Efemp1.

Reviewer #1 (Significance (Required)):

The wide range of assays the authors perform to assess visual deficits is commendable. Such a comprehensive approach ranging from anatomical, behavioral and electrophysiological assays is poised to identify changes that could otherwise be overlooked. Given the increasing use of zebrafish as models of ocular diseases, this study provides a solid roadmap of the types of analysis possible. This work should be interesting to researchers in the field of myopia research and to basic vision researchers interested in using the zebrafish as a model organism.

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

Summary: In this study, the authors used the zebrafish model to study efemp1, a gene that was previously found to be associated with myopia. They used CRISPR-Cas9 to create specific efemp1 knockout in the retina in a mosaic manner. They used a few histological and physiological techniques to evaluate the resulting mutant and found that the efemp1 mutants developed symptoms that are consistent with myopia. The authors further quantified the expression of a few potential target genes in the eye that are potentially implicated in myopia phenotype. The authors also evaluated the differential phenotype of the efemp1 mutant grown in different light conditions that might contribute to myopia.

Major comments:

Overall, the authors have provided convincing evidence of the phenotype created by their efemp1 perturbation. Their experiments were thoroughly done and extensively analyzed. They even discussed some potential shortcomings of their study. Their study is a nice first step towards a better understanding of the efemp1 gene function in ocular growth and in myopia. All my comments below should be addressed by clarifications and discussions and not by any new experiments or projects.

Minor comments:

1. Elaborate the rationale for choosing efemp1 from the original GWAS study for zebrafish investigation. The authors only mentioned that this gene is among the highest in the rank and its role in myopia is not clear. However, there are quite a few other genes in the GWAS study that were ranked as high, if not higher than efemp1.

We thank the reviewer for the suggestion. Firstly, in a previous study, we used the high-throughput zebrafish optomotor response assay coupled with morpholino gene knockdown to screen top-ranked myopia-risk genes from the GWAS study. To use zebrafish as a model, additionally we took into account several other factors including existence of zebrafish orthologues, gene expression in the eye, association of ocular phenotypes with risk genes shown in previous zebrafish studies, fatality of gene depletion and availability of characterized morpholinos to prioritize GWAS-associated risk genes for screening. With significant reduction of OMR responses in efemp1 morphants, efemp1 was selected as a gene of interest for investigation. As our pre-screen is currently an unpublished study, we were not showing the data in the manuscript, but we are happy to show relevant results to the reviewer if requested. To clarify the selection of this gene, we have added a brief statement in the Introduction:

“Our previous study (unpublished) screening GWAS-associated myopia-risk genes with high-throughput optomotor response measurement and morpholino gene knockdown indicated that knockdown of efemp1 in larval zebrafish reduced spatial-frequency tuning function, making efemp1 a candidate gene worth for further investigation for myopia development.” (Line 53–57)

On the other hand, in the Introduction of our manuscript, we indeed had covered that in humans, efemp1 disruptions, with either gain- or loss-of functions, would lead to visual disease, such as Malattia Leventinese, doyne honeycomb retinal dystrophy, juvenile-onset open-angle glaucoma, or high myopia. These also implicated the importance in understanding the role of efemp1 in ocular development.

Elaborate the rationale for choosing retina as the target tissue of efemp1 knockout, especially when the original GWAS study indicated the expression of EFEMP1 is in cornea, RPE, and sclera, but not in retinal cells.

Firstly, efemp1 is expressed in the retina as shown by our immunostaining in zebrafish and in situ hybridization in mouse in a previous study (PMID: 26162006). We have modified the manuscript to clarify this point:

“EFEMP1 is a secreted extracellular matrix glycoprotein widely expressed throughout the human body, especially in elastic fiber-rich tissues, for examples, the brain, lung, kidney and eye including the retina (Livingstone et al., 2020; Mackay et al., 2015).” (Line 51–53)

In future studies it will be interesting to perform similar somatic efemp1 manipulation in other ocular tissues to examine whether this gene has tissue-dependent functions for ocular growth. Nonetheless, our results demonstrated that at the very least retinal efemp1 is involved in ocular development.

Secondly, the rx2 gene is indeed also expressed in the RPE in zebrafish (PMID: 11180949), meaning that there were also RPE cells expressing Cas9 driven by rx2. We have added this detailed to the manuscript:

“In this transgenic zebrafish line, Tg(rx2:Gal4) is expressed specifically in the retina and the RPE (Chuang and Raymond, 2001), due to the retina-specific retinal homeobox gene 2 (rx2) promoter.” (Line 95–97)

Importantly, as myopia generally develops due to dysregulated gene-environment interactions, modification of efemp1 specifically in the light-sensing retina allowed us to investigate the interaction of efemp1 with visual environment. We have added this point to the manuscript:

“In order to investigate the role of the efemp1 gene and its interaction with visual environment, we first generated a zebrafish line with efemp1 modification specifically in the retina (efemp12C-Cas9; Fig 1A), the light-sensing tissue in the eye, using a 2C-Cas9 somatic CRISPR gene editing system (Di Donato et al., 2016).” (Line 92–95)

Discuss possible ways of modifying efemp1 gene in the retina that would be more uniform and would not create mosaicism and/or heterogenous mutations that can complicate downstream characterizations and interpretations as the authors currently experienced.

We appreciate the reviewer’s suggestion. One possible way of generating uniform tissue-specific gene modification is to use the Cre-loxP recombination system. We have modified the Discussion of manuscript as per reviewer’s suggestion:

“To avoid such heterogeneous tissue-specific gene editing, the Cre-LoxP system is an option­: using tissue-specific driven Cre recombination to delete LoxP flanked exons of the target gene.” (Line 482–486)

• Added to discussion –

The authors should elaborate further on the effect of the mosaicism and heterogenous mutations on efemp1, a presumably excreted protein, on regulating the ocular growth.

We appreciate the reviewer’s interesting point of view. However, it is very difficult to identify a regionalized effect of mosaicism and heterogenous mutations of efemp1 on ocular growth even with dissected eyes. It is likely that distribution of Cas9-expressing cells was mosaic but still overall even across the retina. Perhaps in other models that allow controlled regional efemp1 manipulation in the eye, for sample, using gene promoters that present dorsal to ventral gradient, comparisons between modified and unmodified regions in the same eye will help to unravel whether efemp1 regulates eye growth only around the location where it was produced.

How did the downstream genes they studied affect by the messing up of the extracellular Efemp1? Is it through altering the Egf signal transduction?

Throughout the Discussion we have tried to cover how efemp1 disruption affect myopia-associated genes where it is possible by linking our results with literature. However, there were not enough details from the literature showing direct pathways between efemp1 and the tested myopia-risk genes. These will be interesting topics for further investigation. To our knowledge, there is no evidence that myopia-associated genes we analyzed in the study are transduced by Egf signaling.

If possible, discuss the original SNP that was associated with efemp1 and the potential mechanisms through which the SNP affects human EFEMP1; Then, discuss how the study of zebrafish efemp1 mutant can aid our understanding of the human's SNP.

Unfortunately, this information is not available. In the meta-analysis our work is based on Efemp1 ranked highly based on biological and statistical evidence. In figure 5 of Tedje et al., 2018, we can see Efemp1 in the first place. Where available, the annotation (light blue column) would indicate whether the variant was found in exonic, UTR or transcribing RNA. Nothing was identified for Efemp1 – which could mean that it is expressed in regulatory sequencing further away.

Typo: Page 15, Line 299: Loss of this gene "promotes".

Thanks to the reviewer, we have corrected the typo.

Reviewer #2 (Significance (Required)):

This study is an interesting and potentially significant addition to the ophthalmology field, as it conducted an initial characterization of a candidate gene for myopia in zebrafish and observed a relevant phenotype after the gene knockout. Colleagues in the myopia field will find the results interesting. In addition, colleagues in the zebrafish field will find the in-depth characterizations and tools used in the paper very informative.

I have conducted research in the human genetics of ophthalmology, gene expression analysis, zebrafish eye development and diseases. I believe my background allows me to effectively appreciate and evaluate the findings of this manuscript.

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

Summary The authors use a retinal-specific promoter to target zebrafish efemp1 for inactivation to study its effects on the eye. Their use of the DiDonato/del Bene 2C-Cas9 system is a good method to target only cells that express a specific promoter i.e. rx2. Following this (mosaic and transient) targeting of efemp1, the authors describe enlarged eyes and myopia development, as well as reduced spatial visual sensitivity and altered retinal function by ERG analysis. Furthermore, expression levels of egr1, tgfb1a, vegfb, and rbp3 are altered, as well as Timp2 and Mmp2 proteins. Finally, dark-rearing of efemp1 mutant fish is reported to lead to emmetropization, rather than myopia.

Major comments

1. The data presented by the authors are interesting, and likely due to efemp1 disruption in the eye. However, the authors should clarify or explain several points, and improve on experimental rigor. Figure 1 C, D- PCRs are not convincing for loss of efemp1. The authors should consider PCR reactions that would show deletion driven by both CRISPRs, or an RFLP reaction based on conventional PCR that would show differences if individual CRISPRs were effective.

Our zebrafish model is not simply a complete knockout model (please see response to reviewer 1’s comment 1 for details). In our model, even in a retina, there will be different indels in cells that expresses Cas9, including gain- or loss-of-function mutations, or mutations that do not even influence its function. In some cases, even with CRISPR cutting, DNA will recover to be wildtype. Thus, even with FACS to sort for Cas9+ (GFP+) cells, it is not possible to provide evidence for such gene modification using conventional PCR, because as long as there is a unmutated target sequence there will be PCR production. Because of this, headloop PCR as a well-established, highly sensitive approach is specifically suitable for our case.

There needs to be better evidence that efemp1 is being edited (e.g. Western blot, or qPCR).

As described in our response to reviewer 1’s comment 1, due the way efemp1 gene was modified in the retina in our model and the unavailability of suitable commercial antibodies, western blot is currently not an option for us. For qPCR, theoretically it is a way to show genetic modification at the transcriptional level, if combined with FACS from dissected eyes and sgRNA target sites specific primers. However, in reality it is not very practical to perform. First of all, even in our model with more Cas9+ cells, due to the patchy expression, the number of these cells are in fact low in a retina. This means that the number of fish to get enough cells for RNA isolation would be much higher, likely to be hundreds of fish. Moreover, in each clutch the number of fish with higher Cas9+ cell number is generally low, estimated to be only ~5%. Overall, this indicates that a large number of fish are required to even just get one sample for such an experiment. With evidence from headloop PCR and visual phenotype verification (OMR; Fig 1E–H and Fig S1), we believe it is certain that efemp1 gene has been modified. As mentioned also, the ability to identify quantifiable phenotypic differences in this model despite the mosaic Cas9 activity and random indels in different cells is highly suggestive of a full knockout of Efemp1 in the eye causing an even larger phenotype.

The data in Figure 7 are not convincing that EFEMP1 protein levels are substantially reduced in mutants.

This is expected. Please see response to reviewer 1’s comment 2.

Why are efemp12C-Cas9 eyes smaller with normal lighting? (Figure S2)

Fig S2 showed that efemp1*2C-Cas9 fish have smaller eye size than control fish only at 2 weeks of age. As shown by our survival data (Fig 2C), fish with more severe gene modification (implicated by more GFP+ cells, GFP+++ fish) are possibly died by 4 weeks of age, likely due to severe deficits in visually driven predation and subsequently nutrition deficiency. These fish thus gradually develop smaller size of the body including the eye with age, compared to control fish. Therefore, it makes senses that overall mutant fish have smaller eyes at 2 weeks of age but as GFP+++ fish die by 4 weeks, the group averaged eye size returned to a level similar to control fish. The fish survived are likely the ones that have mild mutations, which allow them to remain some levels of vision for feeding and develop without discernibly smaller eye size. Because there was variability of eye size in zebrafish caused by either development or gene manipulation, we used a relative calculation (ratio of retinal radius to lens radius) as a myopia index for comparison.

The clustering of datapoints in Figure 2B, 4B, overlaps extensively between control and mutant, and it is not easy to be sure that the high significance scores (***) are accurate.

We thank the reviewer for pointing out this concern. Though data points overlapped to some levels, in general difference between group means were apparent and the range that they deviate (i.e., mean ± SEM) were barely overlap. We realise it was difficult to see the SEM error bars, as they were so close to the mean, that they were hard to distinguish. We have adjusted our figures for clearer visualization of the error bars. Hopefully this will better show how far apart the data are as reflected by the significance scores.

The authors should consider discussing whether loss of efemp1 is developmental only, or sustained. rx2 is likely to be switched off after development, and retinal cells that arise after the rx2:Gal4 ceases to be active will have a normal quotient of efemp1.

Genetic modification in our mutant model is sustained. It is true that rx2 is only transiently expressed during early development, but once gDNA in a cell was modified by a CRISPR editing event driven by the 2C-Cas9 system, it remains throughout cell divisions (the same mutation would be copied during DNA synthesis) and cell lifetime. In addition, it has been showed that in adult teleost activation of rx2 in retinal stem cells in the retinal ciliary marginal zone determines its fate to form retinal neurons (PMID: 25908840). Therefore, in new neurons derived from retinal stem cells in the adult zebrafish retina, there is expression of rx2 to drive the 2C-Cas9 system for genetic modification. We have added relevant details to the Result section:

“Despite the mosaicism, the mutations resulted from the 2C-Cas9 system in retinal cells is expected to be sustained. Also, in adult teleost, activation of rx2 in retinal stem cells in the retinal ciliary marginal zone determines its fate to form retinal neurons (Reinhardt et al., 2015). This suggested that in new neurons derived from retinal stem cells in the adult zebrafish retina, there may be expression of rx2 to drive the 2C-Cas9 system for genetic modification.” (Line 108–116)

The authors should also consider a more detailed discussion of the mechanism mediated by/through efemp1 that alters retinal function and expression of other genes.

We appreciate the reviewer’s suggestion. It is possible to add more detailed discussion to the manuscript for potential mechanistic links, but ultimately such content would be highly speculative and may lead to over-interpretation of the data. Moreover, a comprehensive overview of detailed mechanisms of how efemp1 may alter retinal function and expression of relevant genes will require space and significantly lengthen the manuscript, with however only minimal improvement. Therefore, we believe it is reasonable to only touch the most relevant as we did for the manuscript.

Finally, since a full mouse knockout of efemp1 exists (Daniel et al, 2020), it is not clear why a retinal-specific zebrafish model would give better insight into the phenotype.

There are several advantages of our 2C-Cas9 zebrafish model. Firstly, with a retinal specific modification of the efemp1 gene, we are able to rule out systematic effect. Essentially our focus is the role of efemp1 in specifically ocular development. Secondly, with their smaller size, rapid development, high reproductivity, and ease of genetic and environmental manipulations, zebrafish allow us to perform large-scale high-throughput investigation with different genetic and environmental combinations. Furthermore, by changing the promoter that drives Gal4 expression in our model, we can target precisely different retinal neuron subtypes to characterize which and how different visual circuits are involved.

Minor comments

"Myopia is the most common ocular disorder" is overly broad and needs qualifiers.

We appreciate the reviewer’s rigorousness. However, myopia is in fact the most common ocular disorder around the world. We have mentioned in the Introduction that “Myopia (short-sightedness) is now the most common visual disorder, and is predicted to impact approximately half of the world population by 2050 (Holden et al., 2016).” Therefore, we believe a qualifier is appropriate.

Line 36 - what ocular changes cannot be easily managed?

We thank the reviewer’s suggestion. We have modified the Introduction manuscript to add some examples:

“Although considered manageable with optical correction, the development of high levels of myopia (or pathological myopia) brings with it ocular changes that promote eye diseases that cannot be easily managed (glaucoma, cataract, myopic maculopathy, etc.) (Hayashi et al., 2010; Ikuno, 2017; Marcus et al., 2011).” (Line 34–37)

Why does loss of retinal efemp1 cause reduced OMR response? Unlikely to be refractive error at this stage.

We have modified the Discussion as per the reviewer’s concern:

“We noticed that although 5 dpf efemp12C-Cas9 fish overall were not myopic relative to efemp1+/+ fish (Fig 2B), they showed reduced spatial-frequency tuning function (Fig 1E–H). This phenotype, if not due to refractive error, can be a result of altered visual processing, as aberrant extracellular matrix caused by efemp1 disruption may lead to dysfunctional synapses (Dityatev and Schachner, 2006).” (Line 491–494)

Which Timp2 (Timp2a or Timp2b) is visualized in Figure 7?

Thanks to the reviewer for raising this point. We have added relevant details to the Methods:

“The anti-TIMP2 antibody was developed based on human TIMP2. In a previous study this antibody was showed to label for zebrafish TIMP2a (Zhang et al., 2003). As similarity of zebrafish TIMP2b to human TIMP2 is much lower than that of zebrafish TIMP2a (60.55% vs. 71.23%), labelling of zebrafish TIM2b is less likely. Yet, we are not able to completely rule out this possibility due to lack of information of the exact immunogen.” (Line 790–794)

Why is the inner retina studied for altered protein expression, but not the rest of the eye? Myopia is primarily driven by growth of the outer retinal/sclera.

The reason why we focused on the inner retina is that in our study, prominent expression differences of our proteins of interest between groups were mainly noticed on the inner but not outer retina. We agree that the outer retina is a key driver for visually regulated ocular growth, yet the inner retina also plays a crucial role. There is abundant evidence that the inner retina is involved in development of ocular refraction. For examples, Cx36, Egr1 and dopamine pathways in the inner retina have been reported to be associated with regulation of ocular refraction (PMID: 10412059; PMID: 28602573; PMID: 25052990; PMID: 32547367). We believe it is reasonable to focus on the inner retina, were we observed robust quantifiable expression for the tested proteins in our case.

Reviewer #3 (Significance (Required)):

• General assessment: This study uses retinal-specific inactivation of efemp1 with a clever methodology to study its effects on the eye. However, the necessity of these experiments is not well explained, as a full mouse knockout line exists. • Advance: There are some interesting observations about gene expression following efemp1 inactivation, and useful experiments that look at the combination of genetics with environmental conditions on refractive error. This builds on studies by the Hulleman group on efemp1's role in the eye by adding functional information. • Audience: This will be of interest to both basic researchers and clinicians who study genetic influencers of the eye.

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Referee #3

Evidence, reproducibility and clarity

Summary

The authors use a retinal-specific promoter to target zebrafish efemp1 for inactivation to study its effects on the eye. Their use of the DiDonato/del Bene 2C-Cas9 system is a good method to target only cells that express a specific promoter i.e. rx2. Following this (mosaic and transient) targeting of efemp1, the authors describe enlarged eyes and myopia development, as well as reduced spatial visual sensitivity and altered retinal function by ERG analysis. Furthermore, expression levels of egr1, tgfb1a, vegfb, and rbp3 are altered, as well as Timp2 and Mmp2 proteins. Finally, dark-rearing of efemp1 mutant fish is reported to lead to emmetropization, rather than myopia.

Major comments

The data presented by the authors are interesting, and likely due to efemp1 disruption in the eye. However, the authors should clarify or explain several points, and improve on experimental rigor. Figure 1 C, D- PCRs are not convincing for loss of efemp1. The authors should consider PCR reactions that would show deletion driven by both CRISPRs, or an RFLP reaction based on conventional PCR that would show differences if individual CRISPRs were effective. There needs to be better evidence that efemp1 is being edited (e.g. Western blot, or qPCR). The data in Figure 7 are not convincing that EFEMP1 protein levels are substantially reduced in mutants. Why are efemp12C-Cas9 eyes smaller with normal lighting? (Figure S2) The clustering of datapoints in Figure 2B, 4B, overlaps extensively between control and mutant, and it is not easy to be sure that the high significance scores (***) are accurate. The authors should consider discussing whether loss of efemp1 is developmental only, or sustained. rx2 is likely to be switched off after development, and retinal cells that arise after the rx2:Gal4 ceases to be active will have a normal quotient of efemp1. The authors should also consider a more detailed discussion of the mechanism mediated by/through efemp1 that alters retinal function and expression of other genes. Finally, since a full mouse knockout of efemp1 exists (Daniel et al, 2020), it is not clear why a retinal-specific zebrafish model would give better insight into the phenotype.

Minor comments

"Myopia is the most common ocular disorder" is overly broad and needs qualifiers. Line 36 - what ocular changes cannot be easily managed? Why does loss of retinal efemp1 cause reduced OMR response? Unlikely to be refractive error at this stage. Which Timp2 (Timp2a or Timp2b) is visualized in Figure 7? Why is the inner retina studied for altered protein expression, but not the rest of the eye? Myopia is primarily driven by growth of the outer retinal/sclera.

Significance

• General assessment: This study uses retinal-specific inactivation of efemp1 with a clever methodology to study its effects on the eye. However, the necessity of these experiments is not well explained, as a full mouse knockout line exists.
• Advance: There are some interesting observations about gene expression following efemp1 inactivation, and useful experiments that look at the combination of genetics with environmental conditions on refractive error. This builds on studies by the Hulleman group on efemp1's role in the eye by adding functional information.
• Audience: This will be of interest to both basic researchers and clinicians who study genetic influencers of the eye.

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:

In this study, the authors used the zebrafish model to study efemp1, a gene that was previously found to be associated with myopia. They used CRISPR-Cas9 to create specific efemp1 knockout in the retina in a mosaic manner. They used a few histological and physiological techniques to evaluate the resulting mutant and found that the efemp1 mutants developed symptoms that are consistent with myopia. The authors further quantified the expression of a few potential target genes in the eye that are potentially implicated in myopia phenotype. The authors also evaluated the differential phenotype of the efemp1 mutant grown in different light conditions that might contribute to myopia.

Major comments:

Overall, the authors have provided convincing evidence of the phenotype created by their efemp1 perturbation. Their experiments were thoroughly done and extensively analyzed. They even discussed some potential shortcomings of their study. Their study is a nice first step towards a better understanding of the efemp1 gene function in ocular growth and in myopia. All my comments below should be addressed by clarifications and discussions and not by any new experiments or projects.

Minor comments:

• Elaborate the rationale for choosing efemp1 from the original GWAS study for zebrafish investigation. The authors only mentioned that this gene is among the highest in the rank and its role in myopia is not clear. However, there are quite a few other genes in the GWAS study that were ranked as high, if not higher than efemp1.
• Elaborate the rationale for choosing retina as the target tissue of efemp1 knockout, especially when the original GWAS study indicated the expression of EFEMP1 is in cornea, RPE, and sclera, but not in retinal cells.
• Discuss possible ways of modifying efemp1 gene in the retina that would be more uniform and would not create mosaicism and/or heterogenous mutations that can complicate downstream characterizations and interpretations as the authors currently experienced.
• The authors should elaborate further on the effect of the mosaicism and heterogenous mutations on efemp1, a presumably excreted protein, on regulating the ocular growth. How did the downstream genes they studied affect by the messing up of the extracellular Efemp1? Is it through altering the Egf signal transduction?
• If possible, discuss the original SNP that was associated with efemp1 and the potential mechanisms through which the SNP affects human EFEMP1; Then, discuss how the study of zebrafish efemp1 mutant can aid our understanding of the human's SNP.
• Typo: Page 15, Line 299: Loss of this gene "promotes".

Significance

This study is an interesting and potentially significant addition to the ophthalmology field, as it conducted an initial characterization of a candidate gene for myopia in zebrafish and observed a relevant phenotype after the gene knockout. Colleagues in the myopia field will find the results interesting. In addition, colleagues in the zebrafish field will find the in-depth characterizations and tools used in the paper very informative.

I have conducted research in the human genetics of ophthalmology, gene expression analysis, zebrafish eye development and diseases. I believe my background allows me to effectively appreciate and evaluate the findings of this manuscript.

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

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Xie et al investigates the role of efemp1 in mediating ocular growth. Efemp1, a secreted extracellular matrix glycoprotein, was previously identified as a myopia-risk gene in human GWAS studies. Given that myopia is linked to aberrant eye shape, the authors investigated whether and how this gene mediates eye growth. Using a CRISPR based approach in zebrafish the authors knocked out efemp1 specifically in the retina and established that a myopic eye results. They went further and investigated visual function in these mutant fish using the optomotor response and electroretinograms. As dark-rearing in many animal models has been linked to the induction of myopia, the authors examined the effects of a dark-rearing regimen in efemp1 mutants and found surprisingly that they did not show signs of myopia. Lastly, the expression and distribution of several myopia-associated genes was investigated in the retina of efemp1 mutants and following dark-rearing.

The starting point for this study was the generation of a "retina-specific knockout mutant of the efemp1 gene". However, evidence for a 'successful' knockout at the protein level is missing. Immunostaining for Efemp1 in sections of the entire retina from control and mutant fish would have helped here. It is only in Figure 7 B, C that portions of the inner retina from control and efemp12c-Cas9 fish are shown with Efemp1 immunostaining. Control and mutant retinae show slight relative differences in Efemp1 fluorescence levels which are difficult to reconcile with a knock-out scenario. Presumably this phenotype is a result of the mosaic expression of Cas9 (GFP) shown in Fig 1? Can the authors explain the reason for this mosaicism? Given this mosaic expression would one expect Efemp1 immunoreactive areas intermingled with areas devoid of Efemp1 in the mutant retina? Further, do deficits in the various functional assays the authors perform correlate with the degree of mosaicism? In the same vein, in Figure 2 the authors refer to variation in GFP levels in the efemp12c-Cas9. It is not clear whether the authors mean levels of GFP in individual cells or numbers of GFP+ cells. Presumably the latter. Could the authors clarify? In my opinion understanding and characterizing the efemp12c-Cas9 fish thoroughly is key to interpreting the phenotypes the authors show subsequently.

Significance

The wide range of assays the authors perform to assess visual deficits is commendable. Such a comprehensive approach ranging from anatomical, behavioral and electrophysiological assays is poised to identify changes that could otherwise be overlooked. Given the increasing use of zebrafish as models of ocular diseases, this study provides a solid roadmap of the types of analysis possible. This work should be interesting to researchers in the field of myopia research and to basic vision researchers interested in using the zebrafish as a model organism.

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Reply to the reviewers

General response of the authors to the editor and the reviewers:

We thank the reviewers for their feedback, input and questions as these have helped us to (hopefully) improve the manuscript. We have rewritten several sections of the manuscript, moved methodological descriptions from the Results to the Methods section, and added imaging data for two cytoskeletal proteins, Shot and Cofilin/Twinstar, which confirm the predicted differential DV expression. Because the changes to the text were extensive, we did not mark them by track changes (the manuscript would have been illegible), but would be happy to provide an additional version that includes the tracked changes.

We provide below the point-by-point response to each question and comment made by the reviewers. Our text is in blue.

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__Reviewer #1 __

__Evidence, reproducibility and clarity __

__Summary __

This manuscript investigated changes in the proteome and phosphoproteome during dorsovental axis specification in the Drosophila embryo. To model the three regions in the embryo that are relevant for DV axis development, the authors used specific mutations to enrich for a single type of cells (ventral, lateral, or dorsal). The detected proteins and phosphopeptides were clustered according to the region of expression. There were differences between the protein and corresponding phosphopeptide abundance, suggesting that phosphorylation is a regulatory modification in DV axis establishment. Two different mutations that both result in a ventralized phenotype were found to change marker protein expression in different ways. Using inhibition of microtubule polymerization, this study also investigated the role of microtubules in epithelial folding.

__Major comments __

1. Generally, there is a lack of significance testing throughout the manuscript. Simply reporting fold changes can be misleading, if these changes are not significant. Examples:

2. Rigor of the proteomics evidence showing changes for the expected markers is insufficient because no statistical evaluation is provided. Specifically, in Fig. 1D and Suppl Fig 2: are the fold changes statistically significant?

3. Data in Fig. 4F, 5F need to be assessed for significance. There are other instances in the manuscript where significance should be tested.

We did ANOVA testing for all proteome and phosphoproteome data, and the outcome of these analyses is reported in Supplementary Tables 2 and 3. We have added references to significance throughout, wherever possible and relevant and have included a table that summarizes all p values for all comparisons in all of the figures (Supplementary Table 2). However, note that we do our clustering independent of statistical significance, i.e., we include all values, as we explain in the manuscript.

It is difficult to see the value of the obtained dataset for the community, in part because the data are analyzed by a linear model and cluster assignment developed by the authors, which is a somewhat arbitrary representation. Perhaps the authors could explain how their data could be used by other researchers, and maybe even develop an accessible portal for interacting with the data.

We do provide the entire set of data in a formatted Excel Table as Supplementary Tables 3 and 4, which contain common pairwise comparisons and ANOVA tests that allow a researcher without a strong proteomics background to explore the data, and we also provide the raw proteomics datasets deposited in PRIDE, so any interested colleague can re-analyse them in the manner that suits their purposes best.

We analysed the data in the way we did because it takes account of the knowledge from genetics that we have of all these cell populations. This also allowed us to include the important set of proteins and phosphosites that are completely absent from all but one mutant genotype, and would therefore have dropped out of the statistical analyses.

For example, what does it mean biologically that a protein is a member of a specific cluster shown in Fig. 3C? Is there a predictive value in such an assignment, and how does it relate to the main question of DV axis regulation? An example of a novel insight obtained for specific protein(s) would be useful to illustrate the utility of this analysis.

The clusters represent groups of proteins that are present at higher or lower abundance in subsets of cell populations. So, for example, being present in cluster 5 means (Fig. 3C) that this protein is predicted to be more abundant in the mesoderm than elsewhere (which includes being detected ONLY in the mesoderm, like Snail). This clustering therefore is the way for us to find new proteins that conform to these groups.

We provide here the immunostainings of two cytoskeleton-associated proteins that our proteomic analyses predicted to be more abundant in the ectoderm (Cluster 6: dorsal+lateral):

• The actin-microtubule crosslinker Short-stop (Shot), which is seen to be reduced in the mesoderm.
• The actin-severing protein Cofilin/Twinstar, which was also found downregulated in the mesoderm in the work cited in Ref.:10 Gong L. et al., Development (2004). The staining shows that cofilin-GFP is abundant in the entire subapical region of ectodermal cells, but strongly reduced in ventral furrow cells, where it is only retained in a few apical membrane blebs. These proteins are targets for functional analyses in follow-up work.

[Imaging Data for Reviewers]

Figure: Physical cross-sections of fixed embryos showing the enrichment of proteins in the ectoderm (cluster 6: DL). Dorsal is top, ventral is bottom. Scale bar: 50 um Top panel: Staining for short-stop (shot; cyan / grayscale) and snail (yellow) in embryos expressing gap43-mCherry. Bottom panel: staining for discs large (dlg, magenta) and GFP (green / grayscale) in embryos expressing cofilin-GFP (Kyoto protein trap for Cofilin/Twinstar).

Overall, at present the study appears to have limited novelty and mechanistic insight. The data generally align with prior expectations, but it is unclear how this work advances the field.

We were reassured that the data align with previous studies, but as we state in the text, they go well beyond these valuable and important studies in several dimensions. We had made the following assumptions:

1. DV patterning mutants recapitulate biological qualities of DV cell populations and the differential expression of DV fate determinants, as confirmed in Fig. 1 and Fig. 3D.
2. The differential regulation of the proteomes and phosphoproteomes across DV patterning mutants recapitulates the abundances of proteins and phosphosites within DV cell populations of a wildtype embryo. We confirmed this in Fig. 3A and Fig. 5C with the implementation of a linear model for the abundances of detected proteins and phosphosites. The resulting analysis revealed new avenues for future functional studies, as intended. Most of the work on cell shape regulation at the gastrulation stage has focused on actomyosin and a subset of cell adhesion molecules. We have identified networks of proteins and phosphoproteins that may also control gastrulation (Fig. 6 and Supplementary Fig. 5), including microtubules, which were significantly enriched in networks of phosphoproteins (Fig. 7 and Supplementary Fig. 6).

For example, the observed differences between marker proteins in Toll10B vs. spn27A data seem to confirm previous suggestions that spn27A has a stronger ventralizing effect.

This suggestion was made by colleagues who had unpublished observations on a limited number of gene expression patterns that supported their contention. A correlation analysis (see figure below) of our results now shows that proteins with a restricted dorso-ventral pattern change more in spn27Aex mutants than in Toll10B. If we look at the known mesodermal genes such as Snail, Twist, Mdr49 and CG4500 we find them at higher abundance in spn27Aex than Toll10B , while the ectodermal genes Egr, Zen, Dtg, Tsg, Bsk, and Ptr are reduced more strongly in spn27Aex than in Toll10B. This takes the prior observation of a stronger ventralization of spn27Aex from an anecdotal to a systematic analysis.

[Correlation analyses available for reviewers]

Cross-correlation between the fold changes (FCs) in Toll10B/WT vs. spn27Aex/WT for all proteins detected in wildtype, Toll10B and spn27Aex. Each dot is a protein. The green line is the 'identity' function (slope = 1) that would be expected if the FCs for each protein in both ventralized mutants were exactly the same. A set of proteins with restricted dorso-ventral distribution are highlighted in yellow: mesodermal (ventral) and blue: ectodermal (dorsal).

The role of microtubules in epithelial folding in the embryo has also been demonstrated before.

   The role of microtubules in epithelial folding in the *Drosophila *embryo has indeed been examined in three previous studies that studied dorsal fold formation (Ref.: 35, Takeda et al. NCB 2018), ventral furrow formation (VFF, Ref.: 36, Ko et al. JCB 2019), and salivary gland invagination (Booth et al. Dev Cell 2014). These data reveal diverse and non-conservative functional requirements, ranging from acto-myosin contractility during apical constriction (Booth et al. 2014), force transmission and repair of the supracellular contractile network (but not apical constriction per se, Ko et al 2019), to the generation of expansile forces during cell shape homeostasis (Takeda et al 2018). In light of this potentially broad functional spectrum, we sought to compare three epithelial folds that form within the context of gastrulation: ventral furrow, cephalic furrow and dorsal folds. We confirmed that the initiation of VFF was normal, but the final invagination failed, as per Ko et al. 2019, while dorsal fold initiation did not occur (extending conclusions from Takeda et al 2018). In contrast, cephalic furrow formation, though delayed, did not require microtubules. We also revealed a novel commonality of MT function. Specifically, prior to the initiation of all three epithelial folds, proper nuclear positioning requires MTs. We additionally discovered novel membrane abnormalities in two distinct types of blebs during ventral furrow and dorsal fold formation, respectively. Thus, our data provide insights into the roles of microtubules during epithelial folding that go beyond prior work.

The shown phosphorylation changes (if they are significant) for Toll and Cactus are difficult to explain. In Suppl Fig 2B, E: why is Toll more phosphorylated in the lateralized than in ventralized embryos? (the provided reference 20 does not seem to clarify this).

   These changes are indeed significant (Toll-S871: Vtl vs. WT p = 0.01 , Vsp vs. WT p = 0.002; Cactus-S463: Vsp vs WT p = 0.03); see Supplementary Figure 2B and Supplementary Table 2).

   We have corrected Ref. 20 (Shen B. and Manley J.L., Development 1998). Ref. 20 only shows that Tl is phosphorylated by Pelle (Ref 20: Fig. 6A), although neither the exact position of Tl phosphosite(s) nor the function of Tl phosphorylation were explored in this article. A hallmark of Toll Like Receptor (TLR) regulation is these receptors are subject to tyrosine phosphorylation, which has been widely connected to the regulation of the binding of adaptor proteins to the cytoplasmic tail of TLRs. Both our finding of Serine phosphorylation in Tl, and the differential phosphorylation across cell populations is new, but since we do not know what this particular Serine phosphorylation site does in TLRs in general, we cannot speculate on the meaning of it occurring more in lateral than in ventral cells. In Ref. 20, the authors speculate that Tl phosphorylation by Pelle regulates the association between Tl and Pelle, which then enables Dorsal translocation to the nucleus. It might also be part of a feedback regulation loop, but this is entirely speculative.

Also, certain Cactus phosphorylations appear higher in dorsalized and ventralized embryos, but not in lateralized embryos. Are such changes expected and do they make sense biologically? It is unclear why these phosphorylation data are used to validate the success of the approach.

   The three Cactus phosphosites S463, S467 and S468 were identified and characterised in the work cited in Ref. 19 (Liu Z.P. et al., Genes and Development, 1997), and we used these sites to validate that our approach was sensitive enough to detect known phosphosites in proteins that act on the dorso-ventral patterning pathway specifically at the point of gastrulation (Stage 6 of embryonic development). We also reported in this manuscript the detection of known phosphosites within the Rho-pathway (Fig. 5E,F, Myosin Light Chain: T21, S22; Cofilin: S3).

   Liu Z.P. et al. reported that these three sites map to the Cactus PEST domain, which is required for Cactus degradation in the mesoderm (Belvin M. et al, Genes and Development 1995).  Liu Z.P. et al. also showed that mutating these phosphosites impairs Cactus turnover without affecting the ability of Cactus to bind Dorsal. We can only speculate that the differential phosphorylation across dorso-ventral embryonic cell populations is associated with the regulation of Cactus turnover. Consistent with this, we find Cactus downregulated 1.5 log2 fold in ventralized embryos derived from *spn27Aex/def* mothers. Furthermore, there are a number of signalling pathways that act both in the dorsal and the ventral-lateral domain (e.g., rhomboid/EGF), so it is not surprising to find modifications that are shared by these regions.

The rationale to use a diffusion algorithm for data analysis is not clear. How would the analysis differ if diffusion was not used?

Phosphoproteomics data are often sparse and noisy for a number of reasons (technical; low abundance of phosphorylated peptides compared to other peptides in the cell; biological: not all phosphosites are functional). Network diffusion is a common way used for various data types to boost the signal-to-noise ratio. For example, if from a list of 10 phosphosites, 5 all fall in the same network region or process, and the rest are randomly distributed in the network, chances are that the first region is more representative of the regulated process in that dataset. Using network propagation, the signal coming from the first 5 phosphosites would give a higher score to that network region, marking it as the predominant signal. Our specific implementation, which uses the semantic similarity between nodes to model the edges in the network, further boosts the functional signal by preferentially including nodes that have a higher functional similarity to the initial phosphosites. Our approach therefore allows us to identify the processes that are predominantly ‘active’ in our dataset. We refer the reviewer to our recent preprint for more evidence that this strategy boosts the signal-to-noise ratio in phosphoproteomic datasets and further prioritises more functional phosphosites (https://www.biorxiv.org/content/10.1101/2023.08.07.552249v1). If this approach was not used and we based the identification of relevant processes only on the list of phosphosites, we would have acquired more spurious terms in our functional enrichment analysis. The above preprint also shows that different methods such as the Prize Collecting Steiner Forest algorithm perform worse for phosphoproteomics data.

Generally, the discussion of enriched GO categories presented in Fig. 6 is not rigorous, and it is unclear what biological insight is provided by this figure, probably because the categories are extremely diverse and not clustered in a meaningful way. Despite stating that the work on microtubules came out as a result of proteomic analysis, there is no connection between proteomic data (e.g., data shown in Fig. 6) and microtubule analysis in Fig. 7.

   The connection is between the __phosphoproteomic__ data and the microtubules. The reviewer is correct about the fact there is little connection at the proteomic level with microtubules. Only the diffused network analyses performed on the phosphoproteomic data pointed in this direction. We have improved the writing about this point.

The Discussion section touches on areas of differential protein degradation and mRNA regulation; however, these data are not presented in Results or Figures and so it is difficult to assess the relevance of this analysis.

     We present these data in Figure 6A,B. The network analyses of the clusters showed significant enrichment of cellular component terms that are connected with protein turnover and mRNA regulation. We have added a reference to figure 6 in the Discussion for clarity.

There is insufficient citation of prior literature throughout the manuscript: many statements are lacking proper references.

We have corrected the mistakes and added missing references.

Proteomics data should be deposited into a standard repository that is a member of ProtomeXchange Consortium, such as PRIDE, etc.

All proteomics and phosphoproteomics data have been uploaded to PRIDE:

The raw files for the proteomics and phosphoproteomics experiments were deposited in PRIDE under separate identifiers:

Proteome: Identifier PXD046050 (Reviewer account details: reviewer_pxd046050@ebi.ac.uk, pw: coJ9otiX).

Phosphoproteome: Identifier PXD046192 (Reviewer account details: reviewer_pxd046192@ebi.ac.uk, pw: nvkbwClp).

We have included a statement of raw data availability in the revised version of the manuscript with the PRIDE access information.

__Minor comments __

The text has several typos and should be proof-read, and references to figures and tables should be checked, as some of these are not correct.

We have corrected typos, references to figures and tables in the revised version of the manuscript.

The genotypes for the mutations used in this study should be accompanied by citation describing identification of these mutations and the resulting phenotypes. It would also be helpful to describe the nature of these alleles (molecular lesion, gain vs loss of function, etc.). Some of this information is included in the Discussion, but it would be useful for the reader to learn this early on, when the chosen genotypes are presented.

All this information is and was provided in the methods section and in Table 1, including stock numbers and sources of the stocks. Please see 'Methods, Drosophila genetics and embryo collections'.

2G,H - the X axis should be clearly labeled as logarithmic.

We introduced the log2 label in the X-axis of Fig. 2G,H and any other panel in which this was not expressly made clear.

In Fig. 2G the locations of lines showing fold changes for Twist and Snail seem incorrect. In Fig. 2H the dotted line does not appear to correspond to 50% of the number of phosphosites.

We apologise for these errors, both have been corrected in the revised version of the manuscript.

5D can be improved by adding letters for the coloured clusters.

We have labelled the clusters in Fig. 3B and Fig. 5D. to ease the identification of biologically relevant clusters.

It is unclear if any specific additional insight was obtained using SILAC, the authors may want to discuss this approach and outcomes more.

SILAC has been widely used to deal with the inherent variability of proteomic analyses by introducing a standard that is metabolically labelled, in our case, w1118 flies fed with SILAC yeast were used as the standard. Because the inherent variability is larger in phosphoproteomic experiments (because protein identification is based on phosphorylated peptides only, see Methods), we used SILAC labelling only in the phosphoproteomic experiment.

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__Reviewer #2 __

Evidence, reproducibility and clarity

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The present article by Gomez et al describes a deep proteomics analysis of the proteome and phosphoproteome of embryos mutated for key genes involved in the dorso-ventral axis in Drosophila melanogaster. Overall, this is a nice article showing new insight in this development process. The results are mainly descriptive, yet identifies potential new players in the definition of the dorso-ventral axis.

The generation of mutants for genes found up- or down-regulated in each mutant strain would be a significant addition to this manuscript. But I think in its current form the data brings enough new information on this particular developmental step and would be of interest for the fly community.

My main concern is that the manuscript can be difficult to read and overly convoluted at times even for experts in the field. I would suggest the author move some methodological explanations from the results to the methods section to further detail the goals of some results sections.

We have followed these suggestions and hope we have made the manuscript more easily readable.

As an example, the goal of part 3) « A linear model for quantitative interpretation of the proteomes » is not clear to me. Are the authors comparing the abundance of a protein in the WT versus a theoretical WT in order to determine which fractions of mesoderm, lateral ectoderm and dorsal region are actually present in the WT? (...)

Yes, in part, but the main purpose was to compare how well the theoretical WT, as ‘reconstituted’ from the mutants, corresponds to the observed actual WT (for which we have at least approximate values).

The question that we faced when we started these calculations was: what is the ‘correct’ fraction (or proportion) we should use to weight each protein (or phosphosite) measurement in the mutants. Theoretically, these values should be those that result in the best match between the theoretical WT and the measured WT abundance of each protein (or phosphosite). We knew from actual measurements only the mesodermal fraction, which was determined to be ~20% of the cross-sectional area (Ref. 21: Rahimi, N., et al Dev. Cell. 2016). The neuroectoderm and ectoderm fractions were estimated to be approx. 40% each (Ref.: 22, Jazwinska, A et al. Development 1999), but we lacked an exact number. The systematic exploration of these proportions led us to conclude that indeed both the neuroectoderm and ectoderm fractions should be around 40% each, provided the mesoderm is fixed at 20%. Thus, we used these fractions: D: 0.4 L: 0.4 V: 0.2 for our follow-up analyses.

(...) Or are they using it as a reference to obtain a fold change for the different proteins quantified (in this case why not use the WT?)?

yes, again, in part: as a reference for the EXPECTED fold changes, as would be predicted from the WT.

Since we have moved some of the details of this approach from the main text to the methods section, we have also revised the remaining text and hope it is now clearer.

The proteomics data must be deposited in a public repository. I did not see it stated in the methods section.

All proteomics and phosphoproteomics data have been uploaded to PRIDE; see further comments above in response 13.

The version of the uniprot database is quite old (2016) so is the version of MaxQuant used in this study. Any reasons for that (other than that the analysis was performed in 2016)?

That is indeed the reason.

The data were run on different MS platforms, how did the authors account for the variability in MS signals? What samples were run on which MS platform? Were the WT embryos ran on both?

We measured three replicates, and all five genotypes (four mutant genotypes plus wildtype) for each of the replicates were measured on the same instrument. Specifically, for the whole proteome analyses, replicate one and three of all genotypes were measured on the QExactive Plus instrument and replicate 2 of all genotypes were measured on a QExactive HF-x instrument, as were the phosphoproteomes. So, indeed, the wildtype was measured on both instruments. We thus did not observe instrument-specific bias in the PCA analysis for the proteome data.

We have added this in more detail to the method section:

“Samples of replicate one and three were measured on the QE-Plus system and replicate two was measured on the QE-HF-x system.

For phosphoproteome analysis, (…) Samples of all three replicates were measured on the QEx-HFx system. We added trial samples measured on the QEx-Plus system to increase the phosphosite coverage using the match between runs algorithm.”

In the methods section the authors mention that a high-pH reverse phase fractionation was performed? How many fractions of High-pH reverse phase separation were injected per sample? Was this separation performed for all the samples?

We have adjusted the Methods section regarding the high-pH fractionation by adding the following sentence: “Fractions were collected every 60s in a 96 well plate over 60 min gradient time collecting a total number of 8 fractions per sample.“

Why did the authors used label-free (proteome) and SILAC (phosphoproteome) quantification methods?

See our response to reviewer #1, point 19.

Why is the threshold based on the Q3 of the standard deviation (if I got it right) ? Couldn't they be calculated directly on the distribution of the ratio?

We could also have done it that way.

However, we had wanted also to take into account the variation between the replicates, i.e., the quality of the individual measurements, and we therefore devised the procedure we used, by which the standard deviation of the individual technical replicates enters the calculation with the ratio of the averages, the variability between replicates would have been ignored and we considered it more appropriate to take the more conservative approach. But as it turns out, the cut-off would have ended up being very similar had we calculated it the way the referee suggests,

Page 6: The supplementary figure 2E refers to the protein Cactus and the text to CKII, please modify one or the other to avoid any confusion. Page 7: A dot is missing at the end of the following sentence « if used with the assumed weightings for the populations »

We have corrected these sentences.

Page 19: Replace SppedVac by SpeedVac

We have corrected the error in the manuscript and thank the reviewer for the detailed inspection.

Page 8: why not using a z-score with thresholds directly instead of a -1/+1/0 system and then using the z-score?

Because we wanted to compare the relative changes over wt between mutants (i.e. the similarity between 1 0 0 and 0 -1 -1) rather than the relationship of their absolute values to the wt, and to assign proteins with similar relationships into the same dorso-ventral regulation categories.

The text states this (previously in main text, now in methods):

“The reason for this is that this method takes into account that value sets that represent similar relative differences between the mutants (for example, 0 -1 -1 vs. 1 -1 -1 or 1, 0, 0) are biologically more similar to each other than the raw values indicate. The z-scores for all of these cases would be 1.1547 -0.5774 -0.5774.”

In the abstract it is mentioned that 3,399 proteins are differentially regulated at the proteome level versus 1,699 significantly deregulated at a 10 % FDR in the main text (page 5). Is there a reason for this discrepancy? Same comment for the phosphopeptides.

But we now also see the need to better clarify this point, and we have edited the text accordingly.

The second number refers to those proteins that show statistically significant changes based on ANOVA (1699 proteins).

The first number (3398; note that the number 3399 in the abstract was a typo, now corrected) includes all proteins that were detected in at least 1 replicate in the wildtype (5883/6111) minus those that do not change between the genotypes (2156/6111) and minus all those that change in the same direction in all mutants (329).

This includes proteins that are automatically excluded from ANOVA, i.e., those that are detected only in the wildtype (35/6111 proteins) or in two or more genotypes but only in 1 technical replicate ANOVA negative ones.

As we stated, we did this because it “allows us to include the important group of proteins that show a ‘perfect’ behaviour, like dMyc and WntD, in that they are undetectable in the mutants that correspond to the regions in the normal embryo where these genes are not expressed.”. This 'regulated' set consists of those proteins that exceed the |0.5| fold threshold.

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

This review is a list of many individual critiques. It is unclear what the expertise of the reviewer is (they do not provide the answer to that question in the review form, unlike the other referees), but several of the criticisms are unfounded. Three of the PIs of this work are researchers with extensive experience in Drosophila genetics and early development but are nevertheless confounded by some of the comments made by this referee.

The mutants do not completely "flatten" the embryos.

We do not claim that they do. Nor are the ventral, lateral and dorsal regions in the normal embryo completely ‘flat’ or homogeneous. But the mutants are good representations of the major fates in these regions, as a wealth of published literature from the last 30 years indicates.

For instance, Tl10B broadly expresses snail but also expresses sog in the head. (i.e. Fig 1B - sog and sna expression in Figure 1B mutant backgrounds looks odd.) The sog expression likely relates to a deficiency specific effect.

This ‘sensitive’ area is well known also from other genetic conditions – e.g. partial loss of dorsal and indeed in Spn27A mutants. It is therefore not specific to the Tl10B deficiency but says something about gene interactions in this region. Thus, this cannot be a deficiency-specific effect.

Is sog seen in a Toll10B/+ mutant background?

Yes, it is, and more frequently than in Toll10B/Def.

The deficiency used for the Toll10B experiment is Df(3R)ro80b which is quite large and deletes 14+ genes.

True. However, this does not matter: the mothers are heterozygous, so the genes are not missing, they are present in one wildtype copy! And these mothers are then mated with wildtype fathers, so if expression of these genes were needed in the embryo, then there would be another full wt copy of each. We appreciate that maternal effect genetics can be difficult to follow, but this is all work that has been done a long time ago, and is not the point of this paper at all.

The deficiency used for the spn27A experiment is Df(2L)BSC7 and removes 4+ genes.

Again, this would only matter if these were maternal effect genes that were needed for the establishment of the dorso-ventral axis, and they are not.

Furthermore, the gd9 allele may not be a complete loss of function.

It may not be – but what matters is the well characterized phenotype which has been shown to represent dorsal cell types.

It is possible that the Toll10B allele picked up an accessory dominant mutation.

This again would only matter if it was a dominant AND maternal effect mutation that affects the DV axis in the embryo – and there are very few of these known. And nothing in our analysis of these embryos, with which we have been working on and off over 3 decades and therefore know very well, indicates that our current stock is any different from those we have seen in the past.

Unfortunately, these mutant phenotypes that affect DV and AP patterning mean that conclusions cannot be made that changes in protein relate to DV patterning.

We simply do not understand this statement.

Why do the mutant phenotypes (gene expression patterns and cell morphologies representative of the ventral, lateral and dorsal cell populations) not mean that the proteins downstream of the fate changes correspond to the cell fates?

To get a better view of the ventralized phenotype, the authors should repeat the analysis by ectopically expressing Toll10B using the Gal4-UAS system; UAS-activate Toll transgenes are available.

All Gal4-UAS maternal drivers, even the best and the strongest, result in mosaic expression. Our lab has extensive experience with this system and we know that, for example, the homogeneous, high levels of twist or snail expression that we see in spn or Tl10B embryos cannot be achieved with GAL4.

Fig 1C-F - due to combined AP and DV effects seen with ventralizing mutants, it is important that the authors confirm that cross-section views relate to the middle to posterior of the embryo.

We confirm this.

Costaining with anti-Kr or -Caudal would help to ensure they are assaying the correct AP domain for pure DV effects.

In our view, this is an unnecessary experiment. I know where the middle of the embryo is. If the reviewer does not believe when we say we are showing a section from the middle, they can see that the sections are not from the end region by, for example, the cell number, and the section angles.

The authors refer to reference [60] for stages but there is no information regarding morphological criteria used under the microscope to stage the embryos.

We have now added more detail in the methods section:

Briefly. using a Zeiss binocular, the embryos were individually hand-selected on wet agar which made the embryos semi-transparent, allowing the assessment of a range of morphological features, of which at least some are visible in each of the mutants:

• Yolk distance to embryonic surface: distinguishes between early (stage 5a) and late cellularisation (stage 5b).
• Yolk distribution within the embryo: identification of large embryonic movements of the germ band (e.g.: Initiation of germ band extension, marking the initiation of stage 7). In DV patterning mutants this is seen as twisting of the embryo.
• Change in the outline of the dorsal-posterior region: polar cell movement from the posterior most region of the embryo (stage 5a/b) to stage 6a/b.
• Formation of the cephalic and dorsal folds: identification of stage 6 (initiation of cephalic fold) and stage 7 (dorsal folds). The combined use of these morphological criteria, together with the synchronised egg collections allows accurate staging of wild type and mutant embryos.

Furthermore, what is stage 6a,b? Stage 6 is not typically divided in two stages nor is it clear what a,b relate to.

We used a generally accepted standard for staging embryos: Campos-Ortega J.A. and Hartenstein V. ‘The embryonic development of Drosophila melanogaster’ book (ref. Nº 60). In this book, they describe the morphological criteria that can be followed in living embryos for proper staging. These stages, with these exact names, are shown on pages 11 and 12 of the 1997 edition (2nd edition).

According to the published timetable of Drosophila development by Foe et al. 1993 (not cited), gastrulating embryos are 200 min or 3 hr 20'. It's unclear if this is the stage that was assayed.

Foe is a beautiful paper, but we did not cite it because the commonly used nomenclature predates it (Campos-Ortega and Hartenstein 1985).

In addition, timing depends on temperature whereas morphological criteria do not.

The mutant embryos likely develop at different rates relative to wildtype. It seems important to provide details about the staging of embryos. If the mutant embryos take longer to gastrulate, for instance, might that also be a factor that impacts the proteome.

As described above, we used a combination of criteria to accurately judge staging. DV patterning embryos could in principle develop faster or slower than wildtype. We performed synchronised egg collections (Methods: Embryo collections) for 15’. Therefore, any developmental timing defect would have become evident based on a difference in the number of embryos entering stage 6 and 7 at the point of visual inspection of the collections. This was not the case.

How many replicates for each genotype? In the text it states, "replicates from the same genotype clustered together (Fig. 2E)....." Similar vague reference for phosphoproteome follows (Fig 2F). It is then stated that it was impossible to determine the experimental source for this variation. Could it relate to differences in timing of samples?

We had given the numbers of replicates in the figure legend but have now also included them in the methods section for more clarity. We did 3 replicates for each genotype in each experiment, with the exception of gd9 and spn27aex mutants, for which we did 2 biological replicates each with 3 replicates, making a total of 6 replicates for these genotypes in the proteomic experiment. We have included an additional clarification in figure legend 2. The number of replicates per genotype per experiment can also be seen from the correlation matrices shown Fig. 2E and 2F, in which the replicates are shown individually. The measurements for each replicate for each genotype within each experiment were reported in Supplementary Tables 2 and 3, 'description' tabs of the worksheets.

The lengthy discussion of ratio estimation on page 7 should be streamlined and made more clear. Are the authors throwing out data and only keeping samples that support their model? This seems like overfitting - if I am understanding correctly, you are selecting the samples that support the "majority of proteins fit the linear model" but this isn't necessarily the case.

No, this is a misunderstanding. We do not select data.

We have rephrased this section, but to explain here briefly: We do not select any samples, we state that the majority of proteins fit the theoretical model (and that is not even surprising, because any protein that does not change across the populations will automatically fit the model). We then discuss why some might NOT fit the model. The model doesn’t need to be supported, it simply is a calculation that allows us to stratify the data.

They call this the 'correct' manner (see section 4 page 7) but it seems like a working model and presumptuous to imply that it is the correct way.

We explained in the text why we refer to this as ‘correct’. It is a matter or definition, not presumption, and we even used quotes to be clear about this. ’Correct’ indicates a combination of values that is consistent with the biological model that the DV mutants are good representations of the corresponding embryonic cell populations in a wild type embryo. We do not in any way ‘throw out’ other data, we just note they don’t fit that model. Clarifications on the concept for the model have been added in various places in the text

Figure 3C - it is confusing to use a circular diagram to show DV inferred position of the 14 clusters as their position on the circle does not correspond to where they are expressed on the embryos. Perhaps a stacked bar graph for 6 different domains would be better.

This figure does not show positions of clusters. It is simply a pie chart, as is stated in the figure legend and as can be seen by the numbers and the corresponding sizes of the sectors. We have tried a stacked representation (shown below), but find it no clearer and have therefore stuck with this very common way of representing quantities, and in particular, proportions. We use the same representation with the same colour schemes in all subsequent figures, so proportions can be compared across figures.

It is very hard to follow the text on page 9.

We have rephrased this section

It is very hard to see the gene expression patterns shown in Fig 4A with the color scheme/scale used.

We appreciate this colour scheme does not correspond to the commonly used dark colour on a light background which would mimic histochemistry to show gene expression. The ‘inferno’ colour scheme was used because it allows better quantitative comparisons between subtly different patterns. However, to make these figures more similar to the types of in situ hybridisations that embryologists are used to seeing, we now use a different representation.

In general, Figure 4 is uninterpretable - in particular, what do the numbers mean on the greyscale circle plots in panel D?

We apologize for having failed to explicitly include the explanation for this in the figure legend. The reader will notice that these numbers add up to the number in the circle to the left, and the numbers indicate the number of proteins showing perfect matches (white), partial overlaps (grey) and mismatches (black). We have improved the graphic representation and added an explanation in the figure legend.

Figure 5A. Why wasn't protein abundance and phosphosites identified from an individual, identical sample?

This was because of the way the project developed over the course of the research, and the protein part was originally intended only as a proof of concept, with the intended focus being the phosphoproteome. We later decided to include a full analysis of the proteome, but did not consider it worthwhile and necessary to repeat the entire laborious and expensive experiment with both analyses being done from the same samples.

How can one be sure that the phosphosites were correctly assigned if the proteins were not detected in the proteome but they were only identified in the phosphosite analysis?

We are not sure we understand this question. The phosphoproteomic analysis identifies phosphopeptides of proteins that in turn allow one to identify the protein itself and the amino acid in that peptide that is phosphorylated. So the identification is done only WITHIN the phosphoproteomic analysis and does not relate directly to the proteomic analysis. This explains why we found some phosphopeptides for which we did not detect the full host protein in the proteomic analysis.

Thus, if a protein was detected only in either of the experiments, this fact doesn’t modify the validity of the result, because the identification was done individually for each experiment.

Page 16 - much discussion about the difference between Spn27A and Toll10b/def mutant background. One has half as much Toll receptor. The phenotype of Toll10b/+ should be examined.

Both genotypes have been extensively examined in the past. Tl10B/def has only one copy of the gene from the mother, and the mutant protein is constitutively active. By putting it over a deficiency, we (and others in the past) made sure that the exclusive source for Tl signalling is from this gain of function Tl allele, and that the wildtype receptor, which would still be activated by the natural ligand in a graded pattern along the DV axis, does not confound the result.

The Tl10B/+ combination creates a less ventralized phenotype which is not more similar to that of spn27Aex/def but in fact less similar.

Page 12 - hard to follow the discussion of modeling (?) presented in Figure 6. The results (bottom of page 12 - #1 "most networks are enriched for cellular components associated with regulation of gene expression" and page 13 #2 - "cytoskleeton emerges as a major target of regulation") seem vague and unsubstantiated. Rhabdomere, P granule, micropyle, autophagosome?

We agree with the reviewer that there are many cellular components that are enriched in the diffused network analyses, many of them unrelated to morphogenesis. We had highlighted this finding on page 12, paragraph 3. Nevertheless, we have rephrased the statements as ‘the heat maps illustrate that most of the enriched cellular components in both experiments were highly enriched with cellular components associated with DNA and RNA metabolism or the regulation of gene expression.’ and have now included numbers.

We think ‘a major target’ for phosphorylation does in fact apply to the cytoskeleton, and we had already supplied the number to substantiate this in the manuscript (14/62).

Readers will be able to evaluate these network analyses based on their own fields of interest or particular questions they may wish to address. We haven’t excluded any cellular component terms.

Figure 7 seems like a separate study.

Why were the phosphopeptides investigated to determine if they relate to phosphorylated proteins? Phosphoantibodies could have been generated for a subset. Instead the manuscript pivots to analysis of microtubules.

We are reporting here one example of a proof-of-concept study that we carried out, chosen based on our own research interests and on available tools and reagents. There are clearly many other avenues that could have been explored and that others may want to explore, but that go well beyond this report. We have made this more explicit in the text.

Page 14 - discussion first paragraph. Please cite ref[10] when discussing the "previous study" otherwise the reader will not understand which study you are referring to until the next paragraph.

We have moved the reference from its current position to the one suggested by the reviewer.

• In general, the study would benefit from more attention to references and citations of prior work. A comparison of this work to the Gong et al. Development 2004 study should be made earlier. This work is cited very early on, namely in the introduction.

• The authors start off saying that no other study has looked at proteins from a spatial perspective. We are unsure what the reviewer refers to. We say precisely the opposite: we indicate that studies have been performed to look at differences in cell populations, including that by the lab of Jon Minden (Gong et al), a highly respected former co-author of one of the current authors (ML). We do state that the technologies at the time did not allow the same depth and temporal resolution as the methods that are available nowadays. For instance, Gong et al. used an excellent and original approach at the time, which however did not detect Snail and Twist in the ventralized mutants.

The only time we say ‘no other study’ is about ‘region-specific post-translational regulation of proteins’ - though we do state in the discussion that Gong et al would have detected some of these cases because they used 2D gels.

• Along these lines, there is another more recent proteomic study from Beati et al. Fly 2020 using similarly staged embryos. How do these other experiments compare to the current ones? As they apparently analyzed proteome and phosphopeptides from an identical sample, are the authors' new data using separate samples consistent? This study is actually about a later stage (stage 8 embryos, post-gastrulation). Again, an excellent study, but not directly relevant to our current analysis. It validates the use of SILAC in Drosophila, although it is not the first study to do this. Furthermore, it looks at a different question and biological process using a mutant, htl, to understand the effect of FGF signalling.

• Furthermore, Adam Martin's lab has been studying microtubule action along the dorsoventral axis (Denk-Lobnig et al 2021) and this work is not cited. Denk-Lobnig et al 2021 is about spatial patterns of myosin and actin and how that is governed genetically on the ventral side of the embryo, pertaining primarily to ventral furrow formation. It does not analyse microtubules nor dorsal-ventral cell populations.

It is possible there may be some confusion with another excellent study from Adam Martin’s lab, in which the role of microtubules is analysed. But this is exclusively in the ventral furrow, and the study did not look at the effect of microtubule depolymerisation on nuclear positioning nor membrane behaviour. We cite this work extensively (Ref.: 36, Ko et al. JCB 2019) and we compare our results to that paper. However, our work here goes beyond this study in that it looks at all cells along the DV axis.

General comments:

Typos throughout. For example, page .4 section heading "dorso-ventral cell..."

We have scanned the entire document for typos.

Font size extremely small - for example see Figure 1A gene names, and 1F magnified view.

We have adjusted the fonts in the main figures.

Scale bars not shown when showing magnified views. For example, see Fig 1E,

We have added these.

Reviewer #3 (Significance (Required)): This study by Gomez et al. uses a proteomic-centered approach to study proteomes associated with cell populations in the embryo that they argue relate to different positions along the dorso-ventral axis. They generate a proteomic resource, though it was unclear how anyone could use the data they produce. There is no searchable database and we have to trust that the authors will ultimately provide such a resource to the community.

All proteomics and phosphoproteomics data have been uploaded to PRIDE. Also see responses to the other referees’ queries about this point.

There is the potential for interesting insights but the work is not presented in a way that is accessible or useful. The presentation needs significant improvement.

We have improved the presentation and way the results are presented as per the suggestion of all reviewers.

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Referee #3

Evidence, reproducibility and clarity

The mutants do not completely "flatten" the embryos. For instance, Tl10B broadly expresses snail but also expresses sog in the head. (i.e. Fig 1B - sog and sna expression in Figure 1B mutant backgrounds looks odd.) The sog expression likely relates to a deficiency specific effect. Is sog seen in a Toll10B/+ mutant background? The deficiency used for the Toll10B experiment is Df(3R)ro80b which is quite large and deletes 14+ genes. The deficiency used for the spn27A experiment is Df(2L)BSC7 and removes 4+ genes. Furthermore, the gd9 allele may not be a complete loss of function. It is possible that the Toll10B allele picked up an accessory dominant mutation. Unfortunately, these mutant phenotypes that affect DV and AP patterning mean that conclusions cannot be made that changes in protein relate to DV patterning. To get a better view of the ventralized phenotype, the authors should repeat the analysis by ectopically expressing Toll10B using the Gal4-UAS system; UAS-activate Toll transgenes are available.

• Fig 1C-F - due to combined AP and DV effects seen with ventralizing mutants, it is important that the authors confirm that cross-section views relate to the middle to posterior of the embryo. Costaining with anti-Kr or -Caudal would help to ensure they are assaying the correct AP domain for pure DV effects.

• The authors refer to reference [60] for stages but there is no information regarding morphological criteria used under the microscope to stage the embryos. Furthermore, what is stage 6a,b? Stage 6 is not typically divided in two stages nor is it clear what a,b relate to. According to the published timetable of Drosophila development by Foe et al. 1993 (not cited), gastrulating embryos are 200 min or 3 hr 20'. It's unclear if this is the stage that was assayed.

• The mutant embryos likely develop at different rates relative to wildtype. It seems important to provide details about the staging of embryos. If the mutant embryos take longer to gastrulate, for instance, might that also be a factor that impacts the proteome.

• How many replicates for each genotype? In the text it states, "replicates from the same genotype clustered together (Fig. 2E)....." Similar vague reference for phosphoproteome follows (Fig 2F). It is then stated that it was impossible to determine the experimental source for this variation. Could it relate to differences in timing of samples?

• The lengthy discussion of ratio estimation on page 7 should be streamlined and made more clear. Are the authors throwing out data and only keeping samples that support their model? This seems like overfitting - if I am understanding correctly, you are selecting the samples that support the "majority of proteins fit the linear model" but this isn't necessarily the case. They call this the 'correct' manner (see section 4 page 7) but it seems like a working model and presumptuous to imply that it is the correct way.

• Figure 3C - it is confusing to use a circular diagram to show DV inferred position of the 14 clusters as their position on the circle does not correspond to where they are expressed on the embryos. Perhaps a stacked bar graph for 6 different domains would be better.

• It is very hard to follow the text on page 9.

• It is very hard to see the gene expression patterns shown in Fig 4A with the color scheme/scale used.

• In general, Figure 4 is uninterpretable - in particular, what do the numbers mean on the greyscale circle plots in panel D?

• Figure 5A. Why wasn't protein abundance and phosphosites identified from an individual, identical sample? How can one be sure that the phosphosites were correctly assigned if the proteins were not detected in the proteome but they were only identified in the phosphosite analysis?

• Page 16 - much discussion about the difference between Spn27A and Toll10b/def mutant background. One has half as much Toll receptor. The phenotype of Toll10b/+ should be examined.

• Page 12 - hard to follow the discussion of modeling (?) presented in Figure 6. The results (bottom of page 12 - #1 "most networks are enriched for cellular components associated with regulation of gene expression" and page 13 #2 - "cytoskleeton emerges as a major target of regulation" ) seem vague and unsubstantiated. Rhabdomere, P granule, micropyle, autophagosome?

• Figure 7 seems like a separate study. Why were the phosphopeptides investigated to determine if they relate to phosphorylated proteins? Phosphoantibodies could have been generated for a subset. Instead the manuscript pivots to analysis of microtubules.

• Page 14 - discussion first paragraph. Please cite ref[10] when discussing the "previous study" otherwise the reader will not understand which study you are referring to until the next paragraph. In general, the study would benefit from more attention to references and citations of prior work. A comparison of this work to the Gong et al. Development 2004 study should be made earlier. The authors start off saying that no other study has looked at proteins from a spatial perspective - but this other study from 2004 did just that. They compared ventralized to lateralized embryos. Along these lines, there is another more recent proteomic study from Beati et al. Fly 2020 using similarly staged embryos. How do these other experiments compare to the current ones? As they apparently analyzed proteome and phosphopeptides from an identical sample, are the authors' new data using separate samples consistent?

General comments:

1. Typos throughout. For example, page .4 section heading "dorso-ventral cell..."

2. Font size extremely small - for example see Figure 1A gene names, and 1F magnified view.

3. Scale bars not shown when showing magnified views. For example, see Fig 1E,F

Significance

This study by Gomez et al. uses a proteomic-centered approach to study proteomes associated with cell populations in the embryo that they argue relate to different positions along the dorso-ventral axis. They generate a proteomic resource, though it was unclear how anyone could use the data they produce. There is no searchable database and we have to trust that the authors will ultimately provide such a resource to the community. Furthermore, Adam Martin's lab has been studying microtubule action along the dorsoventral axis (Denk-Lobnig et al 2021) and this work is not cited. There is the potential for interesting insights but the work is not presented in a way that is accessible or useful. The presentation needs significant improvement.

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Referee #2

Evidence, reproducibility and clarity

The present article by Gomez et al describes a deep proteomics analysis of the proteome and phsophoproteome of embryos mutated for key genes involved in the dorso-ventral axis in Drosophila melanogaster. Overall this is a nice article showing new insight in this development process. The results are mainly descriptive yet identifies potential new players in the definition of the dorso-ventral axis. The generation of mutants for genes found up- or down-regulated in each mutant strain would be a significant addition to this manuscript. But I think in its current form the data brings enough new information on this particular developmental step and would be of interest for the fly community. My main concern is that the manuscript can be difficult to read and overly convoluted at times even for experts in the field. I would suggest the author move some methodological explanations from the results to the methods section to further detail the goals of some results sections. As an example, the goal of the part 3) « A linear model for quantitative interpretation of the proteomes » is not clear to me. Are the authors comparing the abundance of a protein in the WT versus a theoritical WT in order to determine which fractions of mesoderm, lateral ectoderm and dorsal region are actually present in the WT ? Or are they using it as a reference to obtain a fold change for the different proteins quantified (in this case why not use the WT?) ?

Other comments:

• The proteomics data must be deposited in a public repository. I did not see it stated in the methods section.

• The version of the uniprot database is quite old (2016) so is the version of MaxQuant used in this study. Any reasons for that (other than that the analysis was performed in 2016) ?

• The data were run on different MS platforms, how did the authors accounted for the variability in MS signals ? What samples were run on which MS platform ? Where the WT embryos ran on both ?

• In the methods section the authors mention that a high-pH reverse phase fractionation was performed ? How many fractions of High-pH reverse phase separation were injected per sample ? Was this separation performed for all the samples ?

• Why did the authors used label-free (proteome) and SILAC (phosphoproteome) quantification methods ?

• Why are the threshold based on the Q3 of the standard deviation (if I got if right) ? Couldn't they be calculated directly on the distribution of the ratio ?

• Page 6 : The supplementary figure 2E refers to the protein Cactus and the text to CKII, please modify one or the other to avoid and confusion.

• Page 7 : A dot is missing at the end of the following sentence « if used with the assumed weightings for the populations »

• Page 19 : Replace SppedVac by SpeedVac

• Page 8 : why not using a z-score with thresholds directly instead of a -1/+1/0 system and then using the z-score ?

• In the abstract it is mentioned that 3,399 proteins are differentially regulated at the proteome level versus 1,699 significantly deregulated at a 10 % FDR in the main text (page 5). Is there a reason for this discrepancy ? Same comment for the phosphopeptides.

Significance

I think in its current form the data brings enough new information on this particular developmental step and would be of interest for the fly community. My main concern is that the manuscript can be difficult to read and overly convoluted at times even for experts in the field.

Reviewer experise: Drosophila proteomics

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Referee #1

Evidence, reproducibility and clarity

Summary

This manuscript investigated changes in the proteome and phosphoproteome during dorsovental axis specification in the Drosophila embryo. To model the three regions in the embryo that are relevant for DV axis development, the authors used specific mutations to enrich for a single type of cells (ventral, lateral, or dorsal). The detected proteins and phosphopeptides were clustered according to the region of expression. There were differences between the protein and corresponding phosphopeptide abundance, suggesting that phosphorylation is a regulatory modification in DV axis establishment. Two different mutations that both result in a ventralized phenotype were found to change marker protein expression in different ways. Using inhibition of microtubule polymerization, this study also investigated the role of microtubules in epithelial folding.

Major comments

• Generally, there is a lack of significance testing throughout the manuscript. Simply reporting fold changes can be misleading, if these changes are not significant. Examples:

1) Rigor of the proteomics evidence showing changes for the expected markers is insufficient because no statistical evaluation is provided. Specifically, in Fig. 1D and Suppl Fig 2: are the fold changes statistically significant?

2) Data in Fig. 4F, 5F need to be assessed for significance. There are other instances in the manuscript where significance should be tested.

• It is difficult to see the value of the obtained dataset for the community, in part because the data are analyzed by a linear model and cluster assignment developed by the authors, which is a somewhat arbitrary representation. Perhaps the authors could explain how their data could be used by other researchers, and maybe even develop an accessible portal for interacting with the data. For example, what does it mean biologically that a protein is a member of a specific cluster shown in Fig. 3C? Is there a predictive value in such an assignment, and how does it relate to the main question of DV axis regulation? An example of a novel insight obtained for specific protein(s) would be useful to illustrate the utility of this analysis.

• Overall, at present the study appears to have limited novelty and mechanistic insight. The data generally align with prior expectations, but it is unclear how this work advances the field. For example, the observed differences between marker proteins in Toll10B vs. spn27A data seem to confirm previous suggestions that spn27A has a stronger ventralizing effect. The role of microtubules in epithelial folding in the embryo has also been demonstrated before.

• The shown phosphorylation changes (if they are significant) for Toll and Cactus are difficult to explain. In Suppl Fig 2B, E: why is Toll more phosphorylated in the lateralized than in ventralized embryos? (the provided reference 20 does not seem to clarify this) Also, certain Cactus phosphorylations appear higher in dorsalized and ventralized embryos, but not in lateralized embryos. Are such changes expected and do they make sense biologically? It is unclear why these phosphorylation data are used to validate the success of the approach.

• The rationale to use a diffusion algorithm for data analysis is not clear. How would the analysis differ if diffusion was not used? Generally, the discussion of enriched GO categories presented in Fig. 6 is not rigorous, and it is unclear what biological insight is provided by this figure, probably because the categories are extremely diverse and not clustered in a meaningful way.

• Despite stating that the work on microtubules came out as a result of proteomic analysis, there is no connection between proteomic data (e.g. data shown in Fig. 6) and microtubule analysis in Fig. 7. Given the broad range of categories shown in Fig. 6, it is not obvious how the jump to tubulin post-translational modifications and microtubule behavior shown in Fig. 7 was made, which leaves Fig. 7 as a disconnected set of results.

• The Discussion section touches on areas of differential protein degradation and mRNA regulation, however these data are not presented in Results or Figures and so it is difficult to assess the relevance of this analysis. There is insufficient citation of prior literature throughout the manuscript: many statements are lacking proper references. Proteomics data should be deposited into a standard repository that is a member of ProtomeXchange Consortium, such as PRIDE, etc.

Minor comments

• The text has several typos and should be proof-read, and references to figures and tables should be checked, as some of these are not correct.

• The genotypes for the mutations used in this study should be accompanied by citations describing identification of these mutations and the resulting phenotypes. It would also be helpful to describe the nature of these alleles (molecular lesion, gain vs loss of function, etc.). Some of this information is included in the Discussion, but it would be useful for the reader to learn this early on, when the chosen genotypes are presented.

• Fig. 2G,H - the X axis should be clearly labeled as logarithmic. In Fig. 2G the locations of lines showing fold changes for Twist and Snail seem incorrect. In Fig. 2H the dotted line does not appear to correspond to 50% of the number of phosphosites. Fig. 5D can be improved by adding letters for the colored clusters.

• It is unclear if any specific additional insight was obtained using SILAC, the authors may want to discuss this approach and outcomes more.

Significance

General assessment

Strengths: The study uses a good model system (mutations that enrich for a specific type of cells) to investigate the proteome during DV axis establishment. The technical approaches are sound and the raw data are mostly of high quality. Limitations: The lack of significance testing throughout the manuscript makes it difficult to determine whether the stated changes are meaningful. It is unclear how experiments with microtubules are connected to the rest of the story. In its present form, the utility of the data for a broader community is limited, because there is no data analysis portal developed for easy data visualization and interaction, and the data in the supplemental tables are not easily interpretable.

Advance: Overall, this study may serve as a resource for future functional investigation, however limitations in data analysis and presentation currently limit its impact. At present, the advance of this study appears incremental, as it largely agrees with prior observations and does not show novel mechanistic insights in our understanding of DV axis specification. Providing clear examples of how this analysis may result in new understanding and explaining the biological relevance of the findings would help to address this problem.

Audience: Researchers working in the fields of dorsoventral axis specification, Drosophila genetics, developmental biology, proteomics.

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Reply to the reviewers

Manuscript number: RC-2023-02154

Corresponding author(s): Marco, Galardini

1. General Statements

We have carefully read the comments put forward by the two reviewers and we have produced a revised version of the manuscript that we believe addresses all the concerns expressed by the reviewers. In short, we have validated our approach against experimentally derived epistatic coefficients, compared our mutual information (MI) method against one that uses direct coupling analysis (DCA), and experimentally tested three interactions in the spike RBD that we have predicted and which emerged only in summer 2023, thus demonstrating the potential predictive power of this approach. We have also carefully reworded the manuscript to acknowledge the inherent limitation of a method based on MI to identify epistatic interactions. We believe that the revised manuscript is now more robust with these new in-silico and in-vitro validations, and more direct in exposing the advantages (speed) and caveats (higher false-positives) of this approach.

Note: the line numbers referenced in the responses to reviewers below refer to the document in which the changes are highlighted.

Point-by-point description of the revisions

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

Summary: The authors inferred the pairwise epistasis through the Mutual Information provided by the spydrpick algorithm. They claim that the MIs could serve as a real-time identification of the epistatic interactions with the SARS-CoV-2 genomes due to the fast inference and high sensitivities.

Major comments:

1.The authors take a data-driven approach to infer the Mutation Information as the epistatic interactions between the mutations over different sites over SARS-CoV-2 genomes. However, it would be better to specify why this metric is reliable to be used as the representation of the pairwise epistatic interactions, and any theoretical explanations to support this.

We agree that readers should be better informed on why MI can be used to estimate epistatic interactions from genomic data. We have therefore expanded the introduction (lines 93-98), methods (lines 540-543) and discussion (lines 453-457) sections to provide a proper theoretical and practical foundation on the use of a MI-based method. Furthermore, we have expanded the results section to add one additional in-silico validation (lines 244-249, Supplementary Figure 5, and updated Supplementary Figure 8) and an in-vitro one (Figure 5, see also reply to comment 2 from reviewer #2), which we believe give strong support to the MI-based method.

2.The authors claimed that the DCA method requires more computational resources and more time to complete. However, with a proper filtering procedure, the computational time could be reduced heavily. An example is Physical Review E 106 (4), 044409, 2002, in which the DCA was used to investigate the real-time pair-wise interactions (month-to-month). There the DCA results were compared with the correlation analysis. It would be nice to have comparisons of the inferred interactions between MIs and other methods.

We agree that our MI-based approach should be compared against DCA-based methods. The original manuscript had in fact one such comparison (for the 2023-03 dataset, Figure 3C), which indicated a strong correlation between the two methods. To make this result more robust we have computed the DCA values for the complete time-series dataset and measured the correlation with the MI values (Supplementary Figure 4)

We observed a relatively high correlation in estimated values between the two methods, with the exception of three time points, i.e., 2020-11, 2023-02 and 2023-03. We can explain these lower correlations with the low overall sequence diversity observed in the early phase of the pandemic (2020-11) and with the different weighting scheme of our approach, which would significantly alter the dataset when compared to the one used by the DCA method, especially towards the later timepoints (see also the reply to reviewer #2, comment 3, section iv). When those three timepoints are excluded, the two methods show a high degree of correlation, implying that they are comparably suitable in detecting coevolutionary signals.

We have also used the 2nd order coefficients derived from experimental data in Moulana et al., 2022 (10.1038/s41467-022-34506-z) to validate both approaches (see methods, lines 624-631).

The panels which we have combined to create the new Supplementary Figure 5, indicate how both approaches (MI for panel A and C, and DCA for panels B and D) correctly recover the interaction with 2nd order epistatic coefficient > 0.15, based on the odds-ratio metric. Our MI-based approach has, however, a higher recall across multiple time points, which is especially visible comparing panels A and B. The DCA-based method did correctly identify known epistatic interactions, but did so only in sporadic timepoints, even though the distribution of the underlying variants did not change significantly month to month. We believe that the higher recall of the MI-based method has a higher value for genomic epidemiology, at least for SARS-CoV-2.

3.In Figure 1C, the authors show that their spydrpick algorithm provides more pairwise MIs for longer distances, where the outliers are denser than those with short distances. How do we explain this phenomenon?

We thank the reviewer for bringing this point up; we actually think that our data shows the opposite, meaning that we observe a higher proportion of close interactions when normalizing by the number of possible interactions. If we take an arbitrary distance threshold of 1'000 bases to define "close" Vs. "distant" interactions, we observe 194 and 280 interactions, respectively. It is true that distant interactions would be more, but the space of possible interactions is orders of magnitude larger for "distant" interactions, simply by the fact that there are more sites from which interactions can originate. As a crude estimate we can use the combinations between 1,000 sites (499,500 possible interactions) Vs those between 28,903 sites (the full SARS-CoV-2 genome length 29,903 bp minus 1,000, 417,677,253). Based on these estimates we have indeed observed less "close" than "distant" interactions.

Minor comments:

4.The explanations of Fig. 1E could be in more detail. Say, the grey dots in Fig. 1E, which is marked as "other" and such "other"s are dominated here. Why?

We thank the reviewer for pointing out a section where more clarity was needed. We have added the following sentence to the figure legend: "The category "other" indicates positions which are not known to have an impact on affinity to ACE2, immune escape or otherwise flagged as MOI/MOC.". This indicates that predicted interactions involving a site classified as "other" are either false positives or previously undiscovered interactions.

5.On line 210, the authors mentioned that the weights of the old sequences are lower "at around six months (120 days)". It would be better to specify why six months is 120 days instead of 180 days,

We have corrected this mistake and indicated 4 months. We thank the reviewer for spotting this error.

Referees cross-commenting

I agree with what Reviewer #2 presented in the Consults Comments. The authors should present the reasons why MIs can be explained as the epistatic interations between sites as both of us mentioned this point. I checked the other revision points that raised by the Reviewer #2. They would be definetely helpful for enhancing the quality of the manuscript.

Reviewer #1 (Significance (Required)):

The work in the current manuscript is interesting and presented nicely. However, the theoretical foundations that the MIs could be explained as epistatic interactions should be illustrated. Otherwise, the tools would be useful for SARS-CoV-2 and other potential pandemics by different virus.

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

The manuscript proposes an approach to identify epistatic interactions in the SRAR-CoV-2 genome using the large amount of genomic data which accumulated during the COVID pandemics. They argue that due to a relatively low computational cost, this can be done online in any ongoing pandemics nowadays (i.e. in the situation where the viral spreading and evolution are closely monitored by massive sequencing). In principle, this is interesting, but in my opinion the manuscript has some strong problems and will require major rewrighting:

1) In difference to the claims of the manuscript, detected correlation does not necessarily imply epistatic couplings:

• Even in a totally neutral setting, mutations may occur by chance together, and expand due to genetic drift or when ecountering a susceptible population. Equally, to independent muations may spread in different geographic regions, without the double mutant ever arising. Both cases lead to non-zero mutual information.

• In evolution, frequently driver and passenger mutations are observed, in particular in settings of relatively high mutation rate. The passenger will rise in frequency with the driver, without any epistatic coupling.

• The very unequal sequencing across geographic areas will enhance certain variants and leave others undetected. Even if the authors avoid double counting of identical sequences, more small variation is detected when sequencing deeper. The Omicron variant illustrates an extreme case here: it combined a large number of mutations, never detected before, but epistasis is not the most likely explanation, but rather lack of monitoring of the evolutionary path from the ancestral variants to Omicron.

• MI has been criticised because it overestimates the effect of indirecrt correlations in particular in dense epistatic networks. The situation in the spike protein in Fig. 1B seems very dense.

Currently the manuscript does not make any effort to disentangle any of these effects.

Following this (and reviewer 1) comments, we have made a number of changes to the manuscript in order to provide more context into how MI can be used to estimate epistatic interactions and the inherent limitations of this approach. In particular, we have expanded the introduction (lines 93-98), methods (lines 540-543) and discussion (lines 453-457) sections in a way that we believe exposes the limitations of the approach. Despite these limitations, we still believe that a MI-based approach strikes a good balance between speed, ease of implementation, and sensitivity. To further demonstrate this point we have added two additional validations to our results: the first one (in-silico) uses estimated 2nd order epistatic coefficients derived from experimental data (Moulana et al., 2022, 10.1038/s41467-022-34506-z), and the second (in-vitro) our own experimental data on three predicted interactions. The results of the new in-vitro validation have been described in the reply to comment #2 from reviewer 1; in short they show how the MI-based method has comparable sensitivity and specificity as the DCA-based method, and most importantly they allow the recovery of known epistatic interactions across the time period in which they have appeared. The results of the in-vitro validation are discussed in the reply to the next comment from this reviewer, as they directly address the predictive power of our approach: in short, we show how we could also validate these predictions. We think that these new results clearly show how, despite its limitations, the MI-based approach is able to identify bona-fide epistatic interactions, with the advantage of being a simple method to be implemented and with the possibility to be run in real time. For a more detailed discussion of the merits of the MI-based approach over DCA, see the reply to comment #3 from this reviewer.

2) What are the predictive capacities of the approach? Mutual information is bounded from above by the individual site entropies. So high MI can be detected only in highly mutated sites - i.e. in sides for sure already under monitoring. In fact, the sites in Fig. 1B with many links reflect the overall profile of variant frequencies in single sites (i.e. a totally non-epistatic measure) available on Nextstrain, and extracted from the same data sources.

The discussion of the results is very anecdotal and it is not clear to me in how far there is any real prediction in the paper, which might surprise and trigger observation or further analyses.

There is an entire line of related research in estimating and exploiting epistatic couplings in HIV evolution (A Chakraborty, M. Kardar, J. Barton, M MacKay and others) - not cited in the manuscript but relevant for the question how to detect epistatic couplings and what they are good for.

We thank the reviewer for pointing out relevant literature we had not covered in the original manuscript, and which can be used to indicate how epistatic interaction signals can be leveraged when studying viruses. We have added citations to these studies in the introduction (lines 76-78) to provide a better background for our own study. Regarding the broader concern of showing the predictive power of our approach, we had a similar concern after the manuscript was submitted, and we had already planned a "blind" in-vitro validation to put our approach to the test. In order to make this validation as "blind" as possible, we expanded the dataset to include sequences until August 2023. We then selected interactions within the spike RBD with confidence level O4 in at least the last 4 time points and with one position already flagged as either "affinity", "escape" or "other MOI/MOC"

We then selected the top three interactions (446-460, 446-486 and 452-490) for our validation, as they have an outlier confidence O4 in at least the 4 time points, and lower or no prediction before. We also added the known 498-501 interaction as a control (Figure 5, panel B)

We then focused on selecting a set of non-synonymous substitutions to test for their potential epistatic interactions. We decided to select 6 substitutions affecting the 3 predicted interactions based on their frequency in the time points after the cutoff of the original manuscript, shown in Figure 5, panel C.

Of those, L452R/F490S and G446S/F486V are anti-correlated in their frequency and virtually never observed together in our dataset, G446S/F486S is observed at low frequency (87 samples after 2023-05), and G446S/N460H is virtually never observed (5 samples). We chose the anti-correlated pairs to test the potential of the MI method to explain these "avoidance" phenomenon, and the low frequency pairs as a way to test an early warning system for mutation signatures that might rise in the future. We then planned to test the impact of the individual variants, the double variants, both in the wild-type background and in the Q498R/N501Y background as a crude model for the Omicron variant.

We then used a pseudovirus assay to test mutated RBDs across two phenotypes: infectivity (i.e. the ability to infect Vero B4 cells) and immune escape (i.e. antibody neutralization curves). We then tested for the presence of epistatic interactions for the double mutants in both backgrounds using a simple linear model (see Methods, lines 711-727). The results of these in-vitro assays are summarized below (Figure 5, panel E for infectivity, F for immune escape).

Double mutants with a significant (p-value -10) interaction have been highlighted with an asterisk. We confirmed the epistatic interaction for the Q498R/N501H, both for its effect on infectivity and immune escape. For both anti-correlated pairs we found a significant interaction for either the infectivity assay (both) and immune escape (G446S/F486V). In particular, we found that the one hand the G446S/F486V pair induced a large drop in infectivity in the Q498R/N501H background while the double mutant was fairly similar to the immune escape profile of the single G446S variant, thus compensating for the loss of escape shown by the F486V variant alone. We observed the opposite for the L452R/F490S pair in terms of infectivity, with the pair showing a large increase in infectivity in the Q498R/N501H background, an effect we found to be significant. The double mutant had a slightly better immune escape profile than the single mutants, although not significant. From these observations we can hypothesize that the G446S/F486V is anticorrelated for their strong defect in infectivity; we cannot apply the same reasoning for the L452R/F490S pair, whose absence from circulating variants could be ascribed to stochasticity in population dynamics or interactions with other variants. We observed a similar impact of the G446S/F486S and G446S/N460H pairs on infectivity as G446S/F486V; based on these results we could estimate that variants carrying these pairs might have a fitness disadvantage. The inability of unsupervised methods (MI or DCA based) to predict the direction of the effect of course makes it difficult to inform which of the two pairs should be added to a "watchlist", but it would potentially reduce the number of interactions to be tested. We believe that the results of this admittedly small scale in-vitro validation demonstrates the potential of the MI-based approach to flag emerging interactions worthy of further studying. Recent advances in scalability of molecular assays (e.g. 10.1101/2024.03.08.584176) could then be coupled with a real-time system as the one we describe in our manuscript to filter out the more relevant interactions. We have added this forward-looking observation in the discussion as well (lines 465-474).

3) The authors say that more involved methods like the Direct Coupling Analysis with Pseudolikelihood maximisation would be too slow for the analysis, but several papers show the contrary. The paper by Zeng et al. (Ref. [39]) does so very early in the pandemics in 2020, and another uncited paper of the same authors (Physical Review 2022) uses a nearly identical approach to study the time evolution of epistatic couplings (extractions from Gisaid at several times). As one of theit results, they show that their approach is not only feasible, but delivers more stable results than simpler correlation measures like MI.

We thank the reviewer for pointing out a relevant reference we had missed in the initial manuscript. At a general level Zeng et al. take a similar approach to what we have described, namely to divide the data according to the isolation date to look for temporal trends. We however see a few differences that we think are in favor of the approach we describe:

1- Our manuscript covers the time period after the emergence of the Omicron variant, in which epistatic interactions are known and have been characterized and validated experimentally, a crucial requirement for validation. We have also conducted an in-vitro validation on a selected set of predicted interactions (see the reply to the previous comment), which indicates that the method is sound and predictive.

2- We have prepared a cumulative time-series dataset, meaning that each month introduces new sequences on top of the ones already selected from the previous time points. To the best of our knowledge the Zheng et al. dataset has "insulated" sequences at each month. We believe our approach has the advantage of allowing for a higher recall, as it includes a representation of extinct lineages, which may increase diversity at key loci and thus boost the signal. As described in the original manuscript and in the reply to this reviewer's comments "iv" and "v", we have added a weighting scheme in order to reduce the influence of older sequences and increase the relevance of smaller lineages.

3- While we have not tested the DCA implementation used by Zeng et al., and we cannot therefore directly comment on its scalability, we have encountered serious limitations when scaling up the popular plmc C implementation developed by the lab of Deborah Marks. In particular we were unable to successfully run it for datasets with more than ~300k sequences, encountering segmentation faults.

Regarding the third point, while this meant that we could not test the DCA approach on the full dataset, we could still manage to apply it on the time series data, focusing exclusively on the spike (S) gene. As shown above in the reply to reviewer's 1 comment #2, the two methods have a high correlation and are both able to recover known interactions, although with the DCA method having a lower recall. Taken together we believe that the MI-based approach we describe is robust enough to be considered when a tradeoff between speed, ease of implementation and sensitivity has to be struck, which we believe may be the case for a rapid response during a potential future pandemic. We have added more details to the part of the discussion in which the comparison with the DCA-based methods was made to point out how those are still feasible with very large collections of sequences (lines 444-448).

It would therefore be essential that the authors strongly revise their manuscript to show the relaibility of the results, the predictive value of the predicted couplings, and the originality and robustness of the approach.

We believe that our response to both reviewers have addressed these concerns, and as a result we have provided a more nuanced view on the use of MI-based methods in the prediction of epistatic interactions in pandemic viruses. Our wording has been modified to make sure that readers interested in replicating our approach are aware of its strengths (speed, ease of implementation) and limitations.

Furthermore, there are some minor issues in the formulations, which should be corrected

i) "the virus has differentiated into a number of lineages, almost all of which have taken over the whole population..." This is wrong. SARS-CoV-2 has always been very heterogeneous, with diverse variants circulating (the authors use millions of non-redundant sequences), and only very few have become VOIs or VOCs at some point. This image of competition between multiple coexisting strains is much closer to clonal interference than what the authors describe (even if clonal interference does not rely on population structure, which has always been an important element in COVID).

We thank the reviewer for pointing out this error in our observation. We have changed "almost all" to "some", which we agree is more accurate.

ii) The authors say that pseudolikelihood methods would require "aggressive subsampling". This is not true, in machine learning massive training data are frequently used in the context of batch learning, i.e. in each learning epoch a "batch" is sampled from the full data. This leads to stochasticity in learning, but all data are eventually used.

We have reformulated this sentence (lines 85-90) to indicate how batch learning could also be used to make certain methods scalable, with the caveat that they would be more complicated to implement.

iii) The authors say that the download also a phylogenetic tree, but I do not see where it is used.

As indicated in the methods section, we have used the phylogenetic tree for two purposes:

1- To single out high quality sequences from the raw MSA (line 515)

2- To compute the weight of each sequence in the final MSA, as described in line 540-549

iv)The authors use sequence weights as implemented in Ref. [31]. There a weighting at sequence similarity threshold of 90% is used. I would expect that there are no SARS-CoV-2 genomes having accumulated more than 10% of nucleotide mutations, i.e. the weighting procedure would be without any effect.

We realized that the sequence weighting scheme we have used is not described in Pensar et al. (10.1093/nar/gkz656), but rather in the implementation of the spydrpick algorithm used by the panaroo software (Tonkin-Hill et al., 10.1186/s13059-020-02090-4). This weighting scheme is based on the more granular metric that is the patristic distance of each sequence from the root of the tree, divided at each branching point by the number of its terminal leaves. In practical terms this means that sequences belonging to smaller lineages (i.e. with fewer observed samples) will have a larger weight, regardless of a discrete sequence similarity threshold, as was done in the original implementation. We have updated the methods section to clearly indicate that the weighting scheme is that first shown in the panaroo software package (line 543).

v)The authors estimate that they need 10,000-100,000 sequences to estimate MI, but find the epistatic coupling in spike residues 498-501 as soon as 6 double mutants are present, which is a frequency of about 1e-4. The corresponding entropies should be low and in consequence the MI, too.

We thank the reviewer for raising this point, which prompted us to devise a way to better illustrate the sequence weighting scheme we have used. As a side note we also discovered that the number of Omicron sequences at the 2021-11 was actually 7, and not 6 as stated throughout the original manuscript, an error we have now fixed. As described in the methods section we have combined two weights in the time-series analysis: the first one, described in the response to the previous comment, is based on the "density" of the phylogenetic tree, which deflates the contribution of "denser" regions of the tree, and the second reduces the relevance of older sequences. The two weights are then combined multiplicatively. As a result the "real" (i.e. effective) number of sequences harboring a particular double mutation will be different than by just counting their occurrences.

As shown in Supplementary Figure 3, the combination of both weights (first column) leads to an increased effective number of sequences for "younger" samples and those that come from "sparser" regions of the overall phylogenetic tree. This is particularly evident for the middle row (2021-11); the light orange dot, which indicates sequences belonging to the first Omicron lineage to appear in the dataset (BA.1), has an actual N of 7, but an effective N of ~100 (exact value 86), thanks to its "novelty" both in the tree (middle panel) and in terms of time (right panel). We again thank the reviewer for raising this point, which led us to generate this visualization, which will hopefully clarify the rationale for the weighting strategy we have used for moist readers.

vi)The authors say that the public health toll of COVID has been "balanced" by scientific discovery - I would urge the authors to avoid such formulations, which sound cynical.

We agree with the reviewer that this comment might sound cynical and tone-deaf, and have reformulated to indicate that the impact of the pandemic has coincided with an accelerated pace of applied scientific discovery.

Referees cross-commenting

Both reports bring up very similar points (points 1 of both reports, point 2 of Reviewer #1 vs. my point 3) but add partially complementary questions (point 3 of Reviewer #1, my point 2), both related to the interpretation of the data. My report is more severe, but reading the ms I am convinced that the paper requires serious revision. So reports seem coherent but with different degrees of recommendations. However, none of the comments of one reviewer is contradiction to the other reviewer.

Reviewer #2 (Significance (Required)):

While the paper asks interesting questions and wants to make use of the quite unique data which have accumulated during the COVID pandemics, the above mentioned problems raise important questions about the manuscript. It would be essential that the authors strongly revise their manuscript to show the relaibility of the results, the predictive value of the predicted couplings, and the originality and robustness of the approach.

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Referee #2

Evidence, reproducibility and clarity

The manuscript proposes an approach to identify epistatic interactions in the SRAR-CoV-2 genome using the large amount of genomic data which accumulated during the COVID pandemics. They argue that due to a relatively low computational cost, this can be done online in any ongoing pandemics nowadays (i.e. in the situation where the viral spreading and evolution are closely monitored by massive sequencing). In principle, this is interesting, but in my opinion the manuscript has some strong problems and will require major rewrighting:

1. In difference to the claims of the manuscript, detected correlation does not necessarily imply epistatic couplings:
2. Even in a totally neutral setting, mutations may occur by chance together, and expand due to genetic drift or when ecountering a susceptible population. Equally, to independent muations may spread in different geographic regions, without the double mutant ever arising. Both cases lead to non-zero mutual information.
3. In evolution, frequently driver and passenger mutations are observed, in particular in settings of relatively high mutation rate. The passenger will rise in frequency with the driver, without any epistatic coupling.
4. The very unequal sequencing across geographic areas will enhance certain variants and leave others undetected. Even if the authors avoid double counting of identical sequences, more small variation is detected when sequencing deeper. The Omicron variant illustrates an extreme case here: it combined a large number of mutations, never detected before, but epistasis is not the most likely explanation, but rather lack of monitoring of the evolutionary path from the ancestral variants to Omicron.
5. MI has been criticised because it overestimates the effect of indirecrt correlations in particular in dense epistatic networks. The situation in the spike protein in Fig. 1B seems very dense.

Currently the manuscript does not make any effort to disentangle any of these effects. 2. What are the predictive capacities of the approach? Mutual information is bounded from above by the individual site entropies. So high MI can be detected only in highly mutated sites - i.e. in sides for sure already under monitoring. In fact, the sites in Fig. 1B with many links reflect the overall profile of variant frequencies in single sites (i.e. a totally non-epistatic measure) available on Nextstrain, and extracted from the same data sources.

The discussion of the results is very anecdotal and it is not clear to me in how far there is any real prediction in the paper, which might surprise and trigger observation or further analyses. There is an entire line of related research in estimating and exploiting epistatic couplings in HIV evolution (A Chakraborty, M. Kardar, J. Barton, M MacKay and others) - not cited in the manuscript but relevant for the question how to detect epistatic couplings and what they are good for. 3. The authors say that more involved methods like the Direct Coupling Analysis with Pseudolikelihood maximisation would be too slow for the analysis, but several papers show the contrary. The paper by Zeng et al. (Ref. [39]) does so very early in the pandemics in 2020, and another uncited paper of the same authors (Physical Review 2022) uses a nearly identical approach to study the time evolution of epistatic couplings (extractions from Gisaid at several times). As one of theit results, they show that their approach is not only feasible, but delivers more stable results than simpler correlation measures like MI.

It would therefore be essential that the authors strongly revise their manuscript to show the relaibility of the results, the predictive value of the predicted couplings, and the originality and robustness of the approach.

Furthermore, there are some minor issues in the formulations, which should be corrected

i) "the virus has differentiated into a number of lineages, almost all of which have taken over the whole population..." This is wrong. SARS-CoV-2 has always been very heterogeneous, with diverse variants circulating (the authors use millions of non-redundant sequences), and only very few have become VOIs or VOCs at some point. This image of competition between multiple coexisting strains is much closer to clonal interference than what the authors describe (even if clonal interference does not rely on population structure, which has always been an important element in COVID).

ii) The authors say that pseudolikelihood methods would require "aggressive subsampling". This is not true, in machine learning massive training data are frequently used in the context of batch learning, i.e. in each learning epoch a "batch" is sampled from the full data. This leads to stochasticity in learning, but all data are eventually used.

iii) The authors say that the download also a phylogenetic tree, but I do not see where it is used.

iv)The authors use sequence weights as implemented in Ref. [31]. There a weighting at sequence similarity threshold of 90% is used. I would expect that there are no SARS-CoV-2 genomes having accumulated more than 10% of nucleotide mutations, i.e. the weighting procedure would be without any effect.

v)The authors estimate that they need 10,000-100,000 sequences to estimate MI, but find the epistatic coupling in spike residues 498-501 as soon as 6 double mutants are present, which is a frequency of about 1e-4. The corresponding entropies should be low and in consequence the MI, too.

vi)The authors say that the public health toll of COVID has been "balanced" by scientific discovery - I would urge the authors to avoid such formulations, which sound cynical.

Referees cross-commenting

Both reports bring up very similar points (points 1 of both reports, point 2 of Reviewer #1 vs. my point 3) but add partially complementary questions (point 3 of Reviewer #1, my point 2), both related to the interpretation of the data. My report is more severe, but reading the ms I am convinced that the paper requires serious revision. So reports seem coherent but with different degrees of recommendations. However, none of the comments of one reviewer is contradiction to the other reviewer.

Significance

While the paper asks interesting questions and wants to make use of the quite unique data which have accumulated during the COVID pandemics, the above mentioned problems raise important questions about the manuscript. It would be essential that the authors strongly revise their manuscript to show the relaibility of the results, the predictive value of the predicted couplings, and the originality and robustness of the approach.

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Referee #1

Evidence, reproducibility and clarity

Summary The authors inferred the pairwise epistasis through the Mutual Information provided by the spydrpick algorithm. They claim that the MIs could serve as a real-time identification of the epistatic interactions with the SARS-CoV-2 genomes due to the fast inference and high sensitivities.

Major comments:

1. The authors take a data-driven approach to infer the Mutation Information as the epistatic interactions between the mutations over different sites over SARS-CoV-2 genomes. However, it would be better to specify why this metric is reliable to be used as the representation of the pairwise epistatic interactions, and any theoretical explanations to support this.
2. The authors claimed that the DCA method requires more computational resources and more time to complete. However, with a proper filtering procedure, the computational time could be reduced heavily. An example is Physical Review E 106 (4), 044409, 2002, in which the DCA was used to investigate the real-time pair-wise interactions (month-to-month). There the DCA results were compared with the correlation analysis. It would be nice to have comparisons of the inferred interactions between MIs and other methods.
3. In Figure 1C, the authors show that their spydrpick algorithm provides more pairwise MIs for longer distances, where the outliers are denser than those with short distances. How do we explain this phenomenon?

Minor comments: 4.The explanations of Fig. 1E could be in more detail. Say, the grey dots in Fig. 1E, which is marked as "other" and such "other"s are dominated here. Why? 5.On line 210, the authors mentioned that the weights of the old sequences are lower "at around six months (120 days)". It would be better to specify why six months is 120 days instead of 180 days,

Referees cross-commenting

I agree with what Reviewer #2 presented in the Consults Comments. The authors should present the reasons why MIs can be explained as the epistatic interations between sites as both of us mentioned this point. I checked the other revision points that raised by the Reviewer #2. They would be definetely helpful for enhancing the quality of the manuscript.

Significance

The work in the current manuscript is interesting and presented nicely. However, the theoretical foundations that the MIs could be explained as epistatic interactions should be illustrated. Otherwise, the tools would be useful for SARS-CoV-2 and other potential pandemics by different virus.

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Reply to the reviewers

Manuscript number: RC-2024-02371

Corresponding author(s): Elena, Rainero

1. General Statements

We would like to thank both reviewers, for highlighting that our work is a 'careful mechanistic and functional investigation' and that the data are 'clear, convincing and appropriately analysed'. We appreciated that our work was recognised to be important the 'cell signalling, ECM, and migration field' and 'may be translationally relevant'. Below we list how we have addressed or are planning to address all the concerns raised by the reviewers. All the changes are marked in blue in the text.

2. Description of the planned revisions

MAPK11 data in figure 1f (deconvolution).

We agree with the reviewer that this is an important point. MAPK11 was not initially included in the deconvolution list, as it was a weak hit from the screen. We have now used the 4 individual siRNAs which are the components of the smart pool used in the screen, and we measured collagen I internalisation in MDA-MB-231 breast cancer cells. Preliminary data indicate a statistically significant reduction in collagen I uptake in 3 out of 4 sequences tested. The efficiency of the siRNAs in reducing MAPK11 levels will be measured by qPCR.

Show p38 inhibition (WB) for the experiments in which the inhibitors were used.

To assess the efficacy of SB203580 at inhibiting p38 signalling, we will assess the phosphorylation of the p38 target ATF2, as previously described (Ivaska et al., 1999).

Is ECM endocytosis-driven migration linked to the ability of the cells to degrade the endocytosed material in their lysosomes? Or is it more a mechanism of ECM remodelling to enable invasion? [Reviewer 1]. Not clear whether ECM uptake actually fuels/is required for invasion, or whether it is simply a consequence [Reviewer 2].

We thank the reviewers for raising this important point. Indeed, it is possible that ECM uptake impacts on both these processes. To elucidate this, we will treat the cells with Bafilomycin A1, to prevent lysosomal acidification and degradation and assess the migratory ability of MDA-MB-231 cells. If ECM endocytosis-driven migration is an ECM-remodelling mechanism, we expect cell migration not to be affected by the presence of Bafilomycin A1; on the contrary, if ECM lysosomal degradation is required, we expect Bafilomycin A1 treatment to impair cell migration.

What is the faith of the integrin vs ECM ligand?

While we showed that internalised ECM components are degraded in the lysosomes, we do not know the faith of the integrin receptor. To measure integrin a2b1 degradation, we will monitor its levels by Western Blotting in the presence of cycloheximide on both plastic and 1mg/ml collagen I, which drives a2b1 internalisation. In addition, we will measure a2b1 internal pool in the presence of E64d, which we showed prevented the degradation of internalised collagen I.

Mechanistic insight into how these kinases and this specific regulatory subunit of the PP2 phosphatase is involved in this process. What are the targets of these kinases and phosphatase? Do they regulate a2b1-integrin phosphorylation or trafficking?

We don't believe that a2b1 is a target of p38, as we did not find any evidence of this in p38 phosphoproteomic studies, while a2b1 has been reported as an upstream regulator of p38. We agree with the reviewer that including more details on the potential p38 targets modulating ECM uptake and migration would be beneficial. We also agree with the reviewer that performing the extensive phospho-proteomic approach and target validation will constitute an entirely different project and this point should not preclude the publication of this paper. The sodium/proton channel NHE1 has been reported as a p38 target (Khadler et al., 2001; Grenier et al., 2008), and it is also a well-known regulator of macropinocytosis. Therefore, here we will investigate whether NHE1 is also phosphorylated by p38 in our system and whether it is required for ECM uptake and cell migration. We have already established that treatment with the NHE1 inhibitor EIPA significantly reduced ECM uptake in MDA-MB-231 cells (Nazemi et al., 2024). PP2A has been shown to dephosphorylate p38, therefore we will confirm this in our system by measuring p38 levels by western blotting.

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

Controls for the silencing efficiency in the screen are missing.

We used integrin b1 and PAK1 as positive controls in the screen. We have now included the integrin b1 staining in the screening plate, to confirm the knock down efficiency (extended figure 2f). In addition, Western Blotting experiments confirmed a >75% reduction in PAK1 levels upon siRNA transfection (extended figure 2g).

Show p38 inhibition (WB) for the experiments in which the inhibitors were used.

Phospho-p38 WB has been extensively used to assess the efficiency of SB202190 treatment, therefore, we performed similar experiments in MDA-MB-231 and found that treatment with SB202190 almost completely abolished p38 phosphorylation induced collagen I adhesion (figure 3f).

Use more than 1 siRNA for PP2A.

We are now including a heatmap showing the effect of the knock down of the different PP2A subunits on ECM uptake (extended figure 3a,b), demonstrating that PPP2R1A has the strongest effect on ECM uptake. PPP2R1A is a core PP2A subunit and its loss has been shown to destabilise the whole PP2A complex (Kauko et al., 2020). In the deconvolution experiment (figure 1f), we are showing for individual siRNA sequences targeting PPP2R1A.

Okadaic acid has the tendency to detach cells from the ECM.

We agree with the reviewer that this effect could indeed affect the interpretation of our results. We'd like to point out that in this study, we used relatively low concentrations (50nM) compared to some published work (up to 300nM). To assess the effect of okadaic acid on cell morphology, we measure the aspect ratio of MDA-MB-231 and A2780-Rab25 cells migrating on CDM and found that okadaic acid treatment and PPP2R1A downregulation resulted in a similar reduction in aspect ratio, representative of more rounded cells (extended figure 3d-ga,b), but we did not detect cell-ECM detachment. To note, the effect on cell morphology was more profound in the cell migration experiments, where the cells are sparser, compared to the ECM uptake experiments, where the cells are more confluent.

It is quite an overstatement to conclude from a 1-to-1 comparison between NMuMG cells and one cell line derivative of PyMT tumour that "these data indicate that ECM internalisation and degradation is upregulated in invasive breast cancer." Either soften this statement (e.g. 'ECM internalisation was higher in PyMT cancer cells than NMuMG normal breast cells'), or provide experimental evaluation across a range of normal versus cancer cells in vitro and using in vivo systems.

We soften the statement, and we described in more details the evidence that we collected from the MCF10 series of cell lines (non-transformed, non-invasive and metastatic cell lines) in the results and discussion.

It is not clear that the authors are comparing like for like. In extended Data Figure 1A, B, In NMuMG cells, these are islands of cells with tight cell-cell compaction, whereas PyMT1 appear as less adherent and compact cells with discontinuous cell-cell adhesions. While it is still appropriate to compare uptake normalised by area of cells, can the authors provide examination of what the ECM update is upon similar cell states, i.e. when both cell types are colonies versus elongated single or chains of cells? This would delineate whether differences are due to cell-cell contact or not, or bona fide differences in ECM uptake despite such different morphologies.

Similar changes in ECM uptake were observed in the MCF10 series of cell lines, where there is no clear morphological difference between the cell lines, indicating that cell-cell adhesion or elongation do not play a significant role here. We have included a statement about this in the discussion.

Throughout, the authors use cartoons of 3D culture of NMuMG, PyMT1 cells, breast to indicate MDA-MB-231 cells, a picture of a mouse, and a pancreas in attempt to orient the reader. This is very confusing as, for example in Extended Data Fig. 1A, B, these suggest 3-Dimensional spheroid cultures, when these are actually isolated cells or, when what is being demonstrated are not 3-Dimensional, but rather are 2D cells inside ECM.

We apologise for creating confusion with the cartoons, we have now removed all the small diagrams, including cartoons representing normal, DCIS and invasive cells, as well as cartoons representing breast, ovarian, pancreatic and mouse cells. Diagrams have been replaced by adding the name of the cell line, where multiple cell lines are present in the same figure.

Why did the authors perform the screen only two times (not trying to diminish the effort here!), when thrice may have helped with statistical analyses? The authors provide significance values for Reactome pathway assessment. How appropriate it is for the presentation of these from only two independent replicates?

We have now clarified how hits were selected in the methods section, accompanied by references of impactful publication screenings where biological duplicates have been previously used, including Sharma and Rao, Nat Immunol 2009 and Chia et al., Nature 2010.

How have the authors assessed whether, and if so to what extent, their cell segmentation is accurate? Can the authors provide evidence for this? For instance, in Figure 2b, this appears to be error-prone, at least for MDA-MB-231 cells.

We apologise for the confusion caused, we have now clarified how cells are detected in the methods section: Cells were imaged using a 60x Nikon A1 confocal microscope. For these experiments, cells were stained for a membrane protein, which is not shown in the images for better visualisation of the uptake. For live imaging uptake, the outline of the cells was visible, therefore being used to calculate the cell area. Confocal experiments were analysed manually.

*The colour schemes that the authors use throughout are not colourblind friendly, and somewhat difficult to follow even for colour-able readers. *

We apologise that the colours chosen in the plots could be difficult to distinguish for colorblind people. We have now changed the colour from all the superplot graphs in the manuscript, so they are colourblind friendly, we have tested this by using an online website simulator (https://pilestone.com/pages/color-blindness-simulator-1#), which shows how graphs are visualised by the diverse spectrum of colorblind readers.

Extended Data Fig. 3 g,h (ITGA2+ITGB1 KD validation) are not mentioned in the main text.

Thank you for pointing this out. We have now included previous Extended Data Fig. 3g (currently 4g) in the result section. Extended data Fig 3h (β1 integrin knockdown) was mentioned together with Extended data Fig 3a (β1 integrin knockdown on matrigel uptake) to facilitate the reading in section 'ECM internalisation is dependent on α2β1 integrin'.

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

Is the ability to take up ECM dependent on ECM proteolytic degradation?

In our recent publication (Nazemi et al., 2024), we assessed the role of matrix metalloproteases (MMP) in ECM uptake and ECM-dependent cell proliferation by treating MDA-MB-231 cells with the broad spectrum MMP inhibitor GM6001. We found that MMP inhibition did not prevent ECM uptake nor ECM-dependent cell growth, consistent with previous findings in the literature (Yamazaki et al., 2020). We are currently characterising the role of secreted cathepsins in controlling ECM uptake as a separate project in our lab, and preliminary data suggest that they might be involved. We feel this point is outside the scope of the current manuscript.

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Referee #2

Evidence, reproducibility and clarity

Summary

The work presented by Martinez and colleagues encompasses a large-scale screen of kinases that regulate internalisation of fluorescently labelled extracellular matrix. The authors identify a requirement for the collagen receptor a2b1-integrin pair in uptake of fluorescently labelled collagen. From this screen, the authors identify that a2b1-integrin, MAP3K1, MAPK11, and PPP2R1A are required for fluorescently labelled collagen uptake and migration of cancer cells in matrix, suggesting that the process of ECM uptake and migration may perhaps be functionally interdependent, or at least co-occurrent. Data are presented suggesting that these components are also at a higher expression level in breast and pancreatic tumour tissues.

Major comments

General assessment

The work is a well-written and presented, gargantuan effort to identify novel kinase regulators of extracellular matrix internalisation. I want to state at the outset that the data are clear, convincing, and appropriately analysed. Claims of effect are supported by robust statistically quantified effects. Moreover, it is notable that the same kinases required for ECM uptake also are required for migration/invasion, suggesting a link between these. But what is lacking is any demonstration of whether ECM uptake actually fuels/is required for invasion, or whether it is simply a consequence.

That a2b1-integrin is involved suggests that this might be a target of these kinases/phosphatase. However, that a2b1-integrin is required for ECM uptake or migration/invasion is an expected, incremental advance. The identification of MAP3K1, MAPK11, and PPP2R1A provides potential novelty. Unfortunately, what is missing is any mechanistic insight into how these kinases and this specific regulatory subunit of the PP2 phosphatase is involved in this process. What are the targets of these kinases and phosphatase? Do they regulate a2b1-integrin phosphorylation or trafficking? And if so, how? Can you map the phosphorylation target sites, and use phosphomimetic sites on targets to overcome blocks? In the absence of such approaches, the work presents as a huge amount of list building (though extremely well done!), and more and more validation (also well done!) of 'hits', but no depth of how this matters for the cell. One can easily appreciate that such approaches constitute an entirely different project (and should not be used in any way to preclude publication of this paper). However, it does limit the novelty of the findings, beyond excellent validation of hits from a screen. But, work to this level should not simply be background findings for the start of a paper. I fully support the publication of this work as an excellent resource, upon addressing the points below.

It is quite an overstatement to conclude from a 1-to-1 comparison between NMuMG cells and one cell line derivative of PyMT tumour that "these data indicate that ECM internalisation and degradation is upregulated in invasive breast cancer." Either soften this statement (e.g. 'ECM internalisation was higher in PyMT cancer cells than NMuMG normal breast cells'), or provide experimental evaluation across a range of normal versus cancer cells in vitro and using in vivo systems.

It is not clear that the authors are comparing like for like. In extended Data Figure 1A, B, In NMuMG cells, these are islands of cells with tight cell-cell compaction, whereas PyMT1 appear as less adherent and compact cells with discontinuous cell-cell adhesions. While it is still appropriate to compare uptake normalised by area of cells, can the authors provide examination of what the ECM update is upon similar cell states, i.e. when both cell types are colonies versus elongated single or chains of cells? This would delineate whether differences are due to cell-cell contact or not, or bona fide differences in ECM uptake despite such different morphologies.

Throughout, the authors use cartoons of 3D culture of NMuMG, PyMT1 cells, breast to indicate MDA-MB-231 cells, a picture of a mouse, and a pancreas in attempt to orient the reader. This is very confusing as, for example in Extended Data Fig. 1A, B, these suggest 3-Dimensional spheroid cultures, when these are actually isolated cells or, when what is being demonstrated are not 3-Dimensional, but rather are 2D cells inside ECM.

Why did the authors perform the screen only two times (not trying to diminish the effort here!), when thrice may have helped with statistical analyses? The authors provide significance values for Reactome pathway assessment. How appropriate it is for the presentation of these from only two independent replicates?

How have the authors assessed whether, and if so to what extent, their cell segmentation is accurate? Can the authors provide evidence for this? For instance, in Figure 2b, this appears to be error-prone, at least for MDA-MB-231 cells.

Can the authors show in vivo that they can see internalised ECM, such as in sections of breast cancer models, internal pools of ECM in the invasive front of tumours?

Minor comments

The colour schemes that the authors use throughout are not colourblind friendly, and somewhat difficult to follow even for colour-able readers.

Extended Data Fig. 3 g,h (ITGA2+ITGB1 KD validation) are not mentioned in the main text.

Significance

Overall, this is a well performed and presented study, with clearly a huge amount of effort and investigation provided into doing such a screen. The data will be of excellent resource for the cell signalling, ECM, and migration field.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript that authors have investigated the link between cell motility in ECM matrix, cell-ECM adhesion signaling and the ability of cells to endocytose ECM proteins. Through careful mechanistic and functional investigation, including a kinase/phosphatase screen, the authors have uncovered a cancer-relevant a2b1-integrin/P38 MAPK/PP2A phosphatase axis responsible for ECM endocytosis and cell migration. Importantly, the authors demonstrate a role for this pathway in the collagen rich cancer type pancreatic cancer as well as chemotherapy resistant breast cancer. This manuscript has an impressive line up of carefully planned, executed and for the most part well controlled experiments. The data very convincingly demonstrate that ECM uptake via micropinocytosis of a2b1-integrin dependent on PP2A/P38 signaling and regulates migration and invasion in ECM. Importantly, these data seem to be applicable beyond breast cancer, based on the data from other tumor models. Figure 1. The authors have set up a very clever HTS screen looking at ECM uptake. The data look interesting but what seems to be lacking are controls for the silencing efficacy of the top targets in the screen. Alos what is the silencing efficacy of the their positive control PAK1? With the focus on P38 (MAPK11) would be good to have data on this also included in Fig. 1f Extended data fig 2g,h the authors have extended their investigation to the MAPK pathway linked kinases. The data are show for the screen replicates but would be good to show the results for the 2 independent siRNAs similar to fig1 Extended data fig 4. Would be important to show p38-inhibition (phospho-wb) for the experiments where inhibitors are used Extended data figure 5. Please use more than 1 siRNA for PP2A as well (similar to MAPK11). Is the ability of a2b1/p38 axis to take up ECM dependent of proteolytic degradation of the ECM? Is it ECM fragments that are macropinocytosed? Figure 4 and Fig 5. Ocadaic acid treatment has the tendency to detach cells from the ECM. Was this observed here/controlled for ? Figure 6. is the ECM endocytosis driven migration linked to the ability of the cells to degrade the endocytosed material in their lysosomes (to provide nutrients for the cell) ? Or is it more a mechanism of ECM remodeling to enable invasion? Finally, what is the faith of the integrin vs. the ECM ligand? Are both degraded or is the integrin recycled?

Significance

Cell migration and invasion are central regulators of cancer progression. While collagen is the most abundant ECM protein in the cancer stroma, the role of the collagen binding integrins remains poorly understood in the process as much of the works has focused on collagenases or fibronectin and its receptors. Here the authors have carried out an unbiased screen of kinases and phosphatases regulating ECM uptake and uncovered a role for ITGA2/PP2A/p38 signaling. Given the druggability of this pathway and the putative clinical relevance shown here, these data may be translationally relevant

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Reply to the reviewers

Response to reviewer comments on Ramesh et.al and Revision plan

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

In this study the Drosophila orthologue of OCRL, the gene mutated in Lowe syndrome, is knocked out and effects upon whole organism physiology and upon the specific function of nephrocytes, the equivalent of the vertebrate kidney, are analysed. The authors report decreased viability of KO animals, in agreement with previous work, and go on to show that nephrocytes are defective in clearance of material from the hemolymph (equivalent of blood). This is accompanied by altered PIP2 and PI4P levels and perturbed endolysosmal organelles. Nephrocyte-specific KO indicates these changes are cell autonomous. Importantly, the phenotypes can be rescued by re-expression of dOCRL, and the human OCRL also rescues, but not when containing mutations that abrogate lipid phosphatase activity or seen in a human Lowe syndrome patient.

The results are clear and convincing and indicate that the Drosophila OCRL KOs (global and nephrocyte-specific) are good models for understanding OCRL function in the kidney. The findings nicely recapitulate what has been shown in human cell lines and previously published zebrafish and mouse models. In that sense the findings are not unexpected and there is some lack of novelty. Nevertheless, the results here, showing the modelling of OCRL in flies, is important to publish. The fly model also offers certain advantages for future studies e.g. ease of genetics and lack of redundancy, which should prove valuable for such investigations. The paper serves as a very solid framework going forwards.

We thank the reviewer for their positive assessment of our manuscript. We would like to reiterate the novel aspects of our study:

• Lowe syndrome has three key clinical features: brain defect, renal dysfunction, and congenital cataract. Our work is a multiscale analysis of Lowe syndrome in a genetically tractable model organism, Drosophila including analysis of whole animal physiology, renal physiology, and the sub-cellular changes in Drosophila larval nephrocytes. As Drosophila nephrocytes are considered a good model of human renal function, we feel that our study lays the foundation for many future investigations of the renal aspects of the Lowe syndrome phenotype. Prior to this work, there was no Drosophila model of the renal phenotypes in Lowe syndrome.
• As the reviewer correctly points out, the cell biological defects we describe in Drosophila OCRL knockout nephrocytes largely overlaps with that reported in multiple model systems including patient samples, human kidney cell lines, zebrafish larvae and a previous study in Drosophila We feel this is an important strength of this paper as this model can then work overlapping with other existing models. This is important since the Drosophila model is the only one with a single gene encoding for the ocrl/Inpp5b subfamily of 5’-phosphatases (in contrast to humans, mouse, and zebrafish) thus avoiding the complications arising from genetic redundancy.
• Lastly, apart from a couple of studies from the Aguilar lab (done in cell lines), we believe that ours is the first study to look at patient derived mutations in an intact animal model. I only have a few suggestions for improving the manuscript, listed below:

1.) The referencing is quite minimal and more relevant references should be cited. An obvious one is Del Signore et al describing KO of OCRL in flies, and there are others on OCRL on endocytosis that were not cited e.g. Erdmann et al, Nandez et al, Choudhury et al.

There are almost 35 manuscripts on the cellular phenotypes of OCRL, many of them reporting cellular defects in various cell types and model system; indeed, there are 6 papers that mention Drosophila OCRL. It is hard to cite them all. Nevertheless, we will take on board the reviewer’s comment positively and try to cite several more. The paper of Signore et.al on Drosophila OCRL was omitted in error and will be included in the revision.

2.) The figure panels should be presented in the right order in the text, which matches their numbering in the figures.

This will be corrected where needed.

3.) Better description is required in a few places in the text so the reader can follow the experiments. For example, what cells are shown in figure 2? How were the PIP probes expressed? Is the imaging in vivo or ex vivo? In Fig 4, how ere the ex vivo experiments performed?

As already indicated in the figure legend, the cells shown in fig 2 are pericardial nephrocytes and this has been specifically stated at the beginning of the results at line 131. We will now also explicitly state in the fig legend that pericardial nephrocytes are being shown.

To measure the levels of PIP2 at the plasma membrane of pericardial nephrocytes we used the well-established PIP2 reporter, the PH domain of PLCδ tagged to mCherry (UAS PH-PLCδ::mCherry). These reporter probes were expressed in pericardial nephrocytes using Dot-Gal4. We dissected the nephrocytes from larvae and performed live imaging to measure the PIP2 levels. The intensity of these probes at the plasma membrane in the nephrocytes corresponds to the levels of the PIP2. The same strategy was used to measure the levels of PI4P, the probes for PI4P- P4M tagged to GFP were generated in our lab and previously published in Balakrishnan et al., J.Cell.Sci 2018- PMID: 29980590 and Basu et.al Dev.Biol, 2020- PMID: 32194035.

For mbsa and dextran uptake assays, these maybe considered as ex-vivo experiments. They have been described in detail in the materials and methods.

4.) The microscopy images in Figure 4 are too dark__.__

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We will redo these images in grayscale to resolve this issue.

5.) Figure S2A needs some sort of schematic so the reader can understand what is being shown.

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We will include in this manuscript a schematic showing the scheme used to generate the crispr deletion mutant. This has already been published in Trivedi et.al eLife 2020.

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__ __6.) In Fig S2G the PIP2 distribution looks different in the nKO compared to the total KO- more on the PM. Is this a consistent result and what is the explanation if so?

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We believe the reviewer is referring to Fig S2E as there is no Fig S2G. Yes, the reviewer is correct in noting that the levels of PIP2 at the plasma membrane are higher in the nephroKO compared to the germline KO. We believe that the reason for the higher levels of PIP2 in the Nephrocyte specific ko is that this is an acute depletion of OCRL whereas in the germline mutant, over time, adaptation through other mechanisms may have partly restored PIP2 levels. Acute depletion offers limited scope for compensation.

__ __7.) In Fig 7 the expression of phosphatase dead OCRL is barely detectable. This makes the functional data difficult to interpret with any certainty. The authors need to be more circumspect in their description of this data and change the writing accordingly.

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It is not uncommon for kinase and phosphatase dead mutant proteins to be expressed at lower levels than their wild type counterpart; this has been reported many times in the literature. However, we will look through our collection of independent transgenic lines and try to find a line where the phosphatase dead mutant expresses at levels as close to the wild type protein as possible.

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__Reviewer #1 (Significance (Required)):

The results are clear and convincing and indicate that the Drosophila OCRL KOs (global and nephrocyte-specific) are good models for understanding OCRL function in the kidney. The findings nicely recapitulate what has been shown in human cell lines and previously published zebrafish and mouse models. In that sense the findings are not unexpected and there is some lack of novelty. Nevertheless, the results here, showing the modelling of OCRL in flies, is important to publish. The fly model also offers certain advantages for future studies e.g. ease of genetics and lack of redundancy, which should prove valuable for such investigations. The paper serves as a very solid framework going forwards.

We thank the reviewer for their positive assessment of our manuscript. We would like to reiterate the novel aspects of our study:

• Lowe syndrome has three key clinical features: brain defect, renal dysfunction, and congenital cataract. Our work is a multiscale analysis of Lowe syndrome in a genetically tractable model organism, Drosophila including analysis of whole animal physiology, renal physiology, and the sub-cellular changes in Drosophila larval nephrocytes. As Drosophila nephrocytes are considered a good model of human renal function, we feel that our study lays the foundation for many future investigations of the renal aspects of the Lowe syndrome phenotype. Prior to this work, there was no Drosophila model of the renal phenotypes in Lowe syndrome.
• As the reviewer correctly points out, the cell biological defects we describe in Drosophila OCRL knockout nephrocytes largely overlaps with that reported in multiple model systems including patient samples, human kidney cell lines, zebrafish larvae and a previous study in Drosophila We feel this is an important strength of this paper as this model can then work overlapping with other existing models. This is important since the Drosophila model is the only one with a single gene encoding for the ocrl/Inpp5b subfamily of 5’-phosphatases (in contrast to humans, mouse, and zebrafish) thus avoiding the complications arising from genetic redundancy.
• Lastly, apart from a couple of studies from the Aguilar lab (done in cell lines), we believe that ours is the first study to look at patient derived mutations in an intact animal model.

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

The researchers have generated an OCRL knockout Drosophila model and successfully used it to model the kidney dysfunction phenotypes of the rare genetic condition Lowe syndrome. They demonstrate endolysosomal phenotypes consistent with observations reported in other model systems, and illustrate that these translate to disrupted endocytic uptake, and clearing of ingested silver nitrate. In addition, there was a significant effect on growth and development of larvae. Phenotypes could be rescued by expression of human WT OCRL, but not by expression of a patient derived mutant version.

Major comments:

The experiments are generally well performed, logical and support the conclusions made by the authors. It would be nice to observe whether there is actin accumulation on the perturbed endosomal compartments described in Figure 4 as this is a common feature observed in other kidney model systems of the disease, although that is not an essential observation for the story outlined in the paper.

Thanks for the comment. We will attempt to do this subject to the availability of suitable fluorophore combinations.

The methods outlined are clear. N numbers and statistical results however are more opaquely reported. Although the number of replicates is mentioned in the material and methods, they are not mentioned in the figure legends, and at least for the silver nitrate uptake experiment, the N number reported does not seem to match the data points on the bar graph - the material and methods reports the experiment was done three times in triplicate, but there are only two individual data points on the bar graph itself. It is thus unclear what they represent. The colours are also not annotated.

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This will be mentioned clearly in both the figure legends and the materials & methods.

With the phosphoinositide binding domain expression in Fig. 2, panel A image for dOCRL KO looks to be an outlier rather than a picture representing the mean.

Overall, N numbers should be added to all figure legends, specifying X of cells assessed from Y number of pupae. In terms of the statistical analysis, exact p-values should be reported. It should be indicated where any relevant comparisons made were not significant. In places the authors have done so, but not consistently. In particular, it is unclear whether the differences in Figure 7D were statistically tested - no p values are reported in the figure legend and no comparisons are indicated in the figure itself.

This will be done in the revised manuscript.__ __ In Figure 7B, it looks like hOCRL PD is barely expressed so it is hard to interpret the lack of rescue shown in panels C and D

It is not uncommon for kinase and phosphatase dead mutant proteins to be expressed at lower levels than their wild type counterpart; this has been reported many times in the literature. However, will look through our collection of independent transgenic lines and try to find a line where the phosphatase dead mutant expresses at levels as close to the wild type protein as possible.

Minor comments

The length of scale bars needs reporting in the figure legend (or on the figures themselves)

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We will include the scale bars in the figure legend__ __ In figure 2A the cell in the control image is a substantially different shape to the other cells indicated in the figure: I assume this is just natural variation and bears no functional significance?

This is natural variation. Even in a single wild type larva, one typically sees variation in the shape of individual pericardial nephrocytes.

I was confused by what the difference between Sup Fig 2F vs Figure 6A was - is this reporting identical data for Control and Nephrocyte specific KO but just once on a log scale and once not (and in the supplemental with the addition of the whole organism knock-out)?

These are not identical data plotted using two different scales, rather separate data.

Were the authors surprised that the according to the data the nephrocyte specific knock-out elevated PI(4,5)P2 levels more than the whole organism knock-out?

Yes, the reviewer is correct in noting that the levels of PIP2 at the plasma membrane are higher in the nephroKO compared to the germline KO. We believe that the reason for the higher levels of PIP2 in the Nephrocyte specific ko is that this is an acute depletion of OCRL whereas in the germline mutant adaptation through other mechanisms may have partly restored PIP2 levels over time. Acute depletion offers limited scope for compensation.

__ __ For figures 6B-D and 7C-D representative examples of the images used to generate the data shown in the graphs should be added at least as a supplemental figure.

This will be provided

Line 196. Need to cite Sup Fig 1E-F in text Line 214 Need to cite Sup Fig 1I-J in text

We will include it

The figure legend for Figure 7 makes reference to a "Figure 7E" which is not present in the manuscript.

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This will be corrected.

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__Reviewer #2 (Significance (Required)):____ __ This paper describes a fly model that links nephrocyte physiology with molecular mechanism of rare disease significance. The paper characterises nephrocyte function by silver nitrate clearance and clathrin and bulk uptake pathways and links them to phosphoinositide lipid levels. Biosensor expression is used alongside lipid mass spectrometry measurements. The paper goes on to measure the effect of re-expression of the human gene and patient mutations. The paper reinforces existing understanding of the physiological and molecular basis of the human kidney disease.

The nephrocyte phenotype mirrors the proximal tubule kidney phenotype observed in a variety of other models, such as the mouse model. Previous work in Drosophila and in other models needs setting out more thoroughly in the introduction and the advantages of the current work made more obvious. Drosophila has the added advantage of being more genetically tractable as a model than for example the mouse model, and so the similarity of behaviour between the two makes this model useful for the field. However it comes across in the text that this is the first use of Drosophila to examine OCRL when this is not the case. The authors are missing some key references to other work to place their study in context. This is not the first Drosophila model of Lowe syndrome. The authors do mention a study by El Kadhi and colleagues (2011) in passing, however a study from Del Signore and colleagues (2017: PMID 29028801) is missing, as is Mondin et al 2019 PMID: 31118240). Whilst Del Signore et al primarily concerns hemocytes, rather than nephrocytes, several comparable observations were made to the submitted work. The Del Signore paper reports several disruptions to the endolysosomal system in hemocytes, which would be consistent with the observations here in nephrocytes, and it also reports the larval lethality after the 3rd instar stage, again consistent with this study. The authors need to set out how is this paper different to what has previously been done in fly.

We apologise for missing out on citing the work of Signore e.al 2017. This will be done in the revised version.

The discussion lacks sufficient detail on the work done in the humanised mouse model too (Festa et al , 2019). This study is mentioned in passing in the introduction, but needs fuller discussion compared to the fly model and mammalian cell culture and zebrafish larval models that the authors discuss.

We will present a comparative discussion of Festa e.al 2019 in the revised version.

The reviewer expertise is in cell biology of OCRL. Nephrocyte physiology and detailed fly issues are outside reviewer expertise.

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

Summary:

This paper describes a function for the Lowe Syndrome phosphoinositide phosphatase OCRL in Drosophila kidney-like nephrocytes. The authors replicate previous findings that Drosophila ocrl null mutants are larval/pupal lethal, and further show that these null mutants fail to clear heavy metal from their nephrocytes. As previously shown in many cell types including in Drosophila, they find that ocrl mutant nephrocytes exhibit endocytic, endolysosomal, and autophagy defects. These defects are rescued by human OCRL but not an enzymatically inactive version or a patient mutation. Overall, this paper validates Drosophila as a model to explore the endocytic/endolysosomal basis of kidney defects in Lowe Syndrome.

Major comments:

For Figure 2E, ____please do not refer to a non-significant difference____ as a "trend". Trend is a statistical term that refers to patterns found in time series datasets. Datasets below the defined threshold of statistical significance are simply "not significantly different". Overall this figure shows a negative result (no change in PIP2 levels in whole animals, and no effect of rescue), and should be described as such. It is not surprising that whole animal PIP2 levels are unaltered in OCRL mutants as there are other phosphatases such as synaptojanin that may be more important in abundant cell types.

Thank you, we will correct this.

The dot-GAL4 driver used for CRISPR of OCRL is not nephrocyte-specific. It also expresses in salivary glands, lymph glands, and weakly in hemocytes (PMID 12324942). It is therefore possible that some of the phenotypes arise from non-cell-autonomous functions, notably hemocyte activation and systemic inflammatory responses as previously reported for Drosophila ocrl mutants (PMID 29028801). The conclusions about cell autonomy of the phenotype should either be softened, or additional experiments should be done with complementary drivers.

We propose to carry out key nephrocyte phenotypes such as dextran uptake using other Gal4 lines such as AB1 Gal4, Hml Gal4 to rule contributions from salivary glands, lymph gland and hemocytes to the phenotypes seen with Dot-GAL4. We will also check phenotypes with Sns-Gal4 which is also a nephrocyte specific GAL4. This will be included in the revised manuscript.

The very low expression level of the human phosphatase-dead mutant makes it impossible to assess if rescue is due to the mutation or simply to lack of protein. Do similarly low expression levels of the wild type protein rescue?

It is not uncommon for kinase and phosphatase dead mutant proteins to be expressed at lower levels than their wild type counterpart; this has been reported many times in the literature. However, will look through our collection of independent transgenic lines and try to find a line where the phosphatase dead mutant expresses at levels as close to the wild type protein as possible.

Minor comments:

• Specific experimental issues that are easily addressable.

__Additional information is required for image analysis methods to enable replication: __It's not clear what the authors mean by "estimating the ratio of plasma membrane/cytoplasmic fluorescence" (p5 line 132). Why estimating and not measuring? If measured (as suggested by the graphs), details of the image analysis method (eg definition of plasma membrane and cytoplasmic ROI) must be described in such a way that they could be replicated. The only method currently provided is "Raw data of imaging were processed and analyzed using Fiji ImageJ,"

Philosophically, all measurements are at some level an estimate; any measurement is the best estimate of what is under consideration, limited by the technical features of the measurement method being used. If the reviewer insists, we agree to change the word “estimating” to “measuring”. The Padinjat lab has published multiple times on the best possible way of estimating phosphoinositide levels at membranes including plasma membrane levels of PIP2 and PI4P. These methods consider various important factors such as the level of expression of the probe, the size of the cells being measured, method of imaging, plane of the cell being imaged, etc. These methods have been previously published in multiple peer-reviewed papers and described in detail in those studies including imaging parameters, sampling methods and data analysis approaches (Sharma et.al Cell.Reports 2019; PMID: 31091438-Star Methods and Basu et.al Dev.Biol 2020 PMID: 32194035). In this study we have used these methods. In view of the reviewer’s comments, we will cite these papers (one is already cited) and include them in the legends of the relevant figures.

__ __For immunofluorescence, the authors state that mean fluorescence intensity of "EEA-1 and Rab-7 staining was quantified after background subtraction from the maximum projections of the stacks and normalized to the area of nephrocytes." Please detail how background was identified and subtracted.

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The steps were followed for the background subtraction in quantifying the MFI of EEA-1 and Rab7 staining:

1. Open the Raw image in ImageJ Fiji.
2. Make a maximum projections of all the stacks by selecting Image> stack>Z project>select maximum projection.
3. Convert the Max Z projected image to HiLo mode by selecting LUT>HiLO.
4. To subtract the background manually draw an ROI in the image on an area that is devoid of any nephrocytes by selecting the oval selection tool. Six such 6 ROIs were drawn in the background of the image.
5. Now measure the MFI of these 6 background ROIs by selecting Analyze>Measure
6. Copy the MFI of all these 6 backgrounds ROIs into the Excel file and calculate the average MFI of these backgrounds 7 Using this average value of the background MFI in ImageJ select Process>Math>Subtract>Enter the average MFI of the background>Click OK

You can always preview the image with background subtraction. This image has been background subtracted. Post the above streps, we drew an ROI around the nephrocyte border and measured the MFI of the EEA-1/Rab7 staining.

All the measurements with the ROIs have been stored in the server along with the Raw images__. __

__ __ For Figure 3C, 6B, 7D it is not clear why the authors have used the categorical measurement of % of cells with red pixels rather than simply measuring the continuous variable of mean pixel intensity. Can more explanation be provided for this choice?

Our goal here is quantifying the level of AgNO3 in nephrocytes. Since AgNO3 it is not a fluorochrome traditional methods of quantification used for fluorochromes are not applicable as one would encounter the problem of non-linearity and saturating images. Since it is difficult to assess the intensity values from the color brightfield images, we used the following method.

The raw brightfield images are opened in FIJI and are converted to 8-bit images (Image>type>8-bit). The images are then inverted using edit>invert and further converted to 16 color pixel LUT (Image>Lookup table> 16 colours) which shows the distribution and intensity of AgNO3 in the following order from white corresponding to the high intensity of AgNO3 and black being the least intense.

To validate our method, we tested it using Rab5-DN/Rab5-RNAi which shows no uptake of AgNO3 (previously published in PMID: PMC5429992). This experiment showed that our analysis works as expected. __ __ - Are prior studies referenced appropriately?

Referencing of prior studies is extremely inadequate, resulting in inflated claims of novelty. Comments can be found below in the significance section.

We will revise the referencing (more details below).

• Are the text and figures clear and accurate?

Text and figures are ok.

Reviewer #3 (Significance (Required)):

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

The study provides a validated new system in which to study ocrl function in kidney-like cells in flies. There are a few technical and interpretation concerns that should be easily addressed. One main limitation of the study is that it does not provide new mechanistic or physiological insight into how OCRL regulates kidney function. A related major limitation is that the manuscript is not placed in its proper context in the field - these phenotypes have been previously observed in other animal models and also in other cell types in the fly, but the paper does not properly cite that previous literature.

We respectfully reiterate that the title of our paper “A genetic and physiological model of renal dysfunction in Lowe syndrome”

Further we would like to reiterate the last line of the abstract which typically sums up what the paper is about is as follows: “Overall, this work provides a model system to understand the mechanisms by which the sub-cellular changes from loss of OCRL leads to defects in kidney function in human patients.”

Nowhere in the manuscript, neither title, abstract or elsewhere have we claimed to have provided new mechanistic or physiological insight into how OCRL regulates kidney function. However, this study is a very detailed and in-depth description of a model system to stud the renal manifestations of Lowe syndrome using the genetically tractable model system, Drosophila. It will be a solid foundation on which many labs can base future studies, both basic and applied in relation to Lowe syndrome.

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

Referencing of prior studies is extremely inadequate, and many of the claims of novelty are incorrect. The introduction asserts that only cellular studies have been conducted in kidney cells and animals, and that "the relationship of the endolysosomal defects in OCRL depleted cells to the altered physiology of kidney cells of LS patients has not been completely determined". Some of the cited papers (e.g. PMID 30590522) did characterize renal physiology at the level of proteinuria, very similar to the silver clearance described in this paper. Additional but important uncited papers that correlate cellular defects with kidney function include PMID 31676724 and 22680056. The authors should thoroughly acknowledge and reference the previous literature on animal and cellular models of kidney dysfunction upon loss of OCRL.

There are almost 35 manuscripts on the cellular phenotypes of OCRL, many of them reporting cellular defects in various cell types and model system; indeed, there are 6 papers that mention Drosophila OCRL. It is hard to cite them all and, in some cases, reconcile findings between them. Nevertheless, we will take on board the reviewer’s comment positively and try to cite several more.

It is also essential to cite published Drosophila in vivo OCRL literature (PMID 29028801), which is completely omitted. A naïve reader would miss that fly OCRL null mutants have previously been characterized in vivo, and that many of the reported findings are duplicated in this paper, including lethal phase, transgene rescue, and most of the cellular phenotypes (PIP2 levels, endocytic and endosomal defects, lysotracker, and autophagy defects, though in hemocytes rather than nephrocytes, and with some interesting differences that are worth pursuing, such as Rab7 levels). The paragraph on p 9 discussing comparison of Drosophila to other systems completely ignores these previous findings. Further, the current manuscript uses specific fly OCRL tools (antibodies and transgenes) from the previous paper without citation, and the reader would not know to look up how these tools were generated and validated. I have signed this review to note that the previous Drosophila work happens to have been from my group, but objectively any knowledgeable reviewer would recognize that it should have been cited and discussed in this paper. Overall it is a disservice to the field to claim novelty by failing to cite the relevant literature. The introduction and discussion should be extensively revised to put the work in its proper context.

The introduction and discussion will be revised accordingly.

To summarize: previously it was known that defects in endosomal membrane traffic in kidney cells of "humanized" ocrl mice or of zebrafish correlated with defects in renal function. It was also known that Drosophila ocrl null mutants are larval/pupal lethal and that their blood cells exhibit endosomal trafficking defects similar to those shown in the current study. This paper shows for the first time that ocrl null mutants also have endosomal trafficking defects in kidney-like nephrocytes, and show defects in the physiological clearing functions of nephrocytes. Thus, this paper replicates the literature for ocrl function in other cell types in Drosophila and in other animal models, and provides a helpful new experimental system for future mechanistic or therapeutic tests of OCRL function in kidney-like cells. However, it does not provide a mechanistic advance into which of the many cellular phenotypes previously observed (and repeated here) lead to kidney dysfunction.

We would respectfully reiterate the title of our paper “A genetic and physiological model of renal dysfunction in Lowe syndrome”

Further we would like to reiterate the last line of the abstract which typically sums up what the paper is about: “Overall, this work provides a model system to understand the mechanisms by which the sub-cellular changes from loss of OCRL leads to defects in kidney function in human patients.”

Nowhere in the manuscript, neither title, abstract or elsewhere have we claimed to have provided new mechanistic or physiological insight into how OCRL regulates kidney function.

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

This paper will be of interest to researchers studying Lowe Syndrome or membrane traffic in Drosophila nephrocytes.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This paper describes a function for the Lowe Syndrome phosphoinositide phosphatase OCRL in Drosophila kidney-like nephrocytes. The authors replicate previous findings that Drosophila ocrl null mutants are larval/pupal lethal, and further show that these null mutants fail to clear heavy metal from their nephrocytes. As previously shown in many cell types including in Drosophila, they find that ocrl mutant nephrocytes exhibit endocytic, endolysosomal, and autophagy defects. These defects are rescued by human OCRL but not an enzymatically inactive version or a patient mutation. Overall, this paper validates Drosophila as a model to explore the endocytic/endolysosomal basis of kidney defects in Lowe Syndrome.

Major comments:

For Figure 2E, please do not refer to a non-significant difference as a "trend". Trend is a statistical term that refers to patterns found in time series datasets. Datasets below the defined threshold of statistical significance are simply "not significantly different". Overall this figure shows a negative result (no change in PIP2 levels in whole animals, and no effect of rescue), and should be described as such. It is not surprising that whole animal PIP2 levels are unaltered in OCRL mutants as there are other phosphatases such as synaptojanin that may be more important in abundant cell types.

The dot-GAL4 driver used for CRISPR of OCRL is not nephrocyte-specific. It also expresses in salivary glands, lymph glands, and weakly in hemocytes (PMID 12324942). It is therefore possible that some of the phenotypes arise from non-cell-autonomous functions, notably hemocyte activation and systemic inflammatory responses as previously reported for Drosophila ocrl mutants (PMID 29028801). The conclusions about cell autonomy of the phenotype should either be softened, or additional experiments should be done with complementary drivers.

The very low expression level of the human phosphatase-dead mutant makes it impossible to assess if rescue is due to the mutation or simply to lack of protein. Do similarly low expression levels of the wild type protein rescue?

Minor comments:

• Specific experimental issues that are easily addressable.

Additional information is required for image analysis methods to enable replication: It's not clear what the authors mean by "estimating the ratio of plasma membrane/cytoplasmic fluorescence" (p5 line 132). Why estimating and not measuring? If measured (as suggested by the graphs), details of the image analysis method (eg definition of plasma membrane and cytoplasmic ROI) must be described in such a way that they could be replicated. The only method currently provided is "Raw data of imaging were processed and analyzed using Fiji ImageJ,"

For immunofluorescence, the authors state that mean fluorescence intensity of "EEA-1 and Rab-7 staining was quantified after background subtraction from the maximum projections of the stacks and normalized to the area of nephrocytes." Please detail how background was identified and subtracted.

For Figure 3C, 6B, 7D it is not clear why the authors have used the categorical measurement of % of cells with red pixels rather than simply measuring the continuous variable of mean pixel intensity. Can more explanation be provided for this choice? - Are prior studies referenced appropriately?

Referencing of prior studies is extremely inadequate, resulting in inflated claims of novelty. Comments can be found below in the significance section. - Are the text and figures clear and accurate?

Text and figures are ok.

Significance

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

The study provides a validated new system in which to study ocrl function in kidney-like cells in flies. There are a few technical and interpretation concerns that should be easily addressed. One main limitation of the study is that it does not provide new mechanistic or physiological insight into how OCRL regulates kidney function. A related major limitation is that the manuscript is not placed in its proper context in the field - these phenotypes have been previously observed in other animal models and also in other cell types in the fly, but the paper does not properly cite that previous literature. - Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

Referencing of prior studies is extremely inadequate, and many of the claims of novelty are incorrect. The introduction asserts that only cellular studies have been conducted in kidney cells and animals, and that "the relationship of the endolysosomal defects in OCRL depleted cells to the altered physiology of kidney cells of LS patients has not been completely determined". Some of the cited papers (e.g. PMID 30590522) did characterize renal physiology at the level of proteinuria, very similar to the silver clearance described in this paper. Additional but important uncited papers that correlate cellular defects with kidney function include PMID 31676724 and 22680056. The authors should thoroughly acknowledge and reference the previous literature on animal and cellular models of kidney dysfunction upon loss of OCRL.

It is also essential to cite published Drosophila in vivo OCRL literature (PMID 29028801), which is completely omitted. A naïve reader would miss that fly OCRL null mutants have previously been characterized in vivo, and that many of the reported findings are duplicated in this paper, including lethal phase, transgene rescue, and most of the cellular phenotypes (PIP2 levels, endocytic and endosomal defects, lysotracker, and autophagy defects, though in hemocytes rather than nephrocytes, and with some interesting differences that are worth pursuing, such as Rab7 levels). The paragraph on p 9 discussing comparison of Drosophila to other systems completely ignores these previous findings. Further, the current manuscript uses specific fly OCRL tools (antibodies and transgenes) from the previous paper without citation, and the reader would not know to look up how these tools were generated and validated. I have signed this review to note that the previous Drosophila work happens to have been from my group, but objectively any knowledgeable reviewer would recognize that it should have been cited and discussed in this paper. Overall it is a disservice to the field to claim novelty by failing to cite the relevant literature. The introduction and discussion should be extensively revised to put the work in its proper context.

To summarize: previously it was known that defects in endosomal membrane traffic in kidney cells of "humanized" ocrl mice or of zebrafish correlated with defects in renal function. It was also known that Drosophila ocrl null mutants are larval/pupal lethal and that their blood cells exhibit endosomal trafficking defects similar to those shown in the current study. This paper shows for the first time that ocrl null mutants also have endosomal trafficking defects in kidney-like nephrocytes, and show defects in the physiological clearing functions of nephrocytes. Thus, this paper replicates the literature for ocrl function in other cell types in Drosophila and in other animal models, and provides a helpful new experimental system for future mechanistic or therapeutic tests of OCRL function in kidney-like cells. However, it does not provide a mechanistic advance into which of the many cellular phenotypes previously observed (and repeated here) lead to kidney dysfunction. - Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

This paper will be of interest to researchers studying Lowe Syndrome or membrane traffic in Drosophila nephrocytes. - Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am an expert in the cell biology of membrane traffic, Drosophila as a model system, and imaging and image analysis. Avital Rodal Professor of Biology Brandeis University

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Referee #2

Evidence, reproducibility and clarity

The researchers have generated an OCRL knockout Drosophila model and successfully used it to model the kidney dysfunction phenotypes of the rare genetic condition Lowe syndrome. They demonstrate endolysosomal phenotypes consistent with observations reported in other model systems, and illustrate that these translate to disrupted endocytic uptake, and clearing of ingested silver nitrate. In addition, there was a significant effect on growth and development of larvae. Phenotypes could be rescued by expression of human WT OCRL, but not by expression of a patient derived mutant version.

Major comments:

The experiments are generally well performed, logical and support the conclusions made by the authors. It would be nice to observe whether there is actin accumulation on the perturbed endosomal compartments described in Figure 4 as this is a common feature observed in other kidney model systems of the disease, although that is not an essential observation for the story outlined in the paper.

The methods outlined are clear. N numbers and statistical results however are more opaquely reported. Although the number of replicates is mentioned in the material and methods, they are not mentioned in the figure legends, and at least for the silver nitrate uptake experiment, the N number reported does not seem to match the data points on the bar graph - the material and methods reports the experiment was done three times in triplicate, but there are only two individual data points on the bar graph itself. It is thus unclear what they represent. The colours are also not annotated.

With the phosphoinositide binding domain expression in Fig. 2, panel A image for dOCRL KO looks to be an outlier rather than a picture representing the mean.

Overall, N numbers should be added to all figure legends, specifying X of cells assessed from Y number of pupae. In terms of the statistical analysis, exact p-values should be reported. It should be indicated where any relevant comparisons made were not significant. In places the authors have done so, but not consistently. In particular, it is unclear whether the differences in Figure 7D were statistically tested - no p values are reported in the figure legend and no comparisons are indicated in the figure itself.

In Figure 7B, it looks like hOCRL PD is barely expressed so it is hard to interpret the lack of rescue shown in panels C and D.

Minor comments

The length of scale bars needs reporting in the figure legend (or on the figures themselves)

In figure 2A the cell in the control image is a substantially different shape to the other cells indicated in the figure: I assume this is just natural variation and bears no functional significance?

I was confused by what the difference between Sup Fig 2F vs Figure 6A was - is this reporting identical data for Control and Nephrocyte specific KO but just once on a log scale and once not (and in the supplemental with the addition of the whole organism knock-out)? Were the authors surprised that the according to the data the nephrocyte specific knock-out elevated PI(4,5)P2 levels more than the whole organism knock-out?

For figures 6B-D and 7C-D representative examples of the images used to generate the data shown in the graphs should be added at least as a supplemental figure.

Line 196. Need to cite Sup Fig 1E-F in text

Line 214 Need to cite Sup Fig 1I-J in text

The figure legend for Figure 7 makes reference to a "Figure 7E" which is not present in the manuscript.

Significance

This paper describes a fly model that links nephrocyte physiology with molecular mechanism of rare disease significance. The paper characterises nephrocyte function by silver nitrate clearance and clathrin and bulk uptake pathways and links them to phosphoinositide lipid levels. Biosensor expression is used alongside lipid mass spectrometry measurements. The paper goes on to measure the effect of re-expression of the human gene and patient mutations. The paper reinforces existing understanding of the physiological and molecular basis of the human kidney disease.

The nephrocyte phenotype mirrors the proximal tubule kidney phenotype observed in a variety of other models, such as the mouse model. Previous work in Drosophila and in other models needs setting out more thoroughly in the introduction and the advantages of the current work made more obvious. Drosophila has the added advantage of being more genetically tractable as a model than for example the mouse model, and so the similarity of behaviour between the two makes this model useful for the field.

However it comes across in the text that this is the first use of Drosophila to examine OCRL when this is not the case. The authors are missing some key references to other work to place their study in context. This is not the first Drosophila model of Lowe syndrome. The authors do mention a study by El Kadhi and colleagues (2011) in passing, however a study from Del Signore and colleagues (2017: PMID 29028801) is missing, as is Mondin et al 2019 PMID: 31118240). Whilst Del Signore et al primarily concerns hemocytes, rather than nephrocytes, several comparable observations were made to the submitted work. The Del Signore paper reports several disruptions to the endolysosomal system in hemocytes, which would be consistent with the observations here in nephrocytes, and it also reports the larval lethality after the 3rd instar stage, again consistent with this study. The authors need to set out how is this paper different to what has previously been done in fly. The discussion lacks sufficient detail on the work done in the humanised mouse model too (Festa et al , 2019). This study is mentioned in passing in the introduction, but needs fuller discussion compared to the fly model and mammalian cell culture and zebrafish larval models that the authors discuss.

The reviewer expertise is in cell biology of OCRL. Nephrocyte physiology and detailed fly issues are outside reviewer expertise.

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Referee #1

Evidence, reproducibility and clarity

In this study the Drosophila orthologue of OCRL, the gene mutated in Lowe syndrome, is knocked out and effects upon whole organism physiology and upon the specific function of nephrocytes, the equivalent of the vertebrate kidney, are analysed. The authors report decreased viability of KO animals, in agreement with previous work, and go on to show that nephrocytes are defective in clearance of material from the hemolymph (equivalent of blood). This is accompanied by altered PIP2 and PI4P levels and perturbed endolysosmal organelles. Nephrocyte-specific KO indicates these changes are cell autonomous. Importantly, the phenotypes can be rescued by re-expression of dOCRL, and the human OCRL also rescues, but not when containing mutations that abrogate lipid phosphatase activity or seen in a human Lowe syndrome patient.

The results are clear and convincing and indicate that the Drosophila OCRL KOs (global and nephrocyte-specific) are good models for understanding OCRL function in the kidney. The findings nicely recapitulate what has been shown in human cell lines and previously published zebrafish and mouse models. In that sense the findings are not unexpected and there is some lack of novelty. Nevertheless, the results here, showing the modelling of OCRL in flies, is important to publish. The fly model also offers certain advantages for future studies e.g. ease of genetics and lack of redundancy, which should prove valuable for such investigations. The paper serves as a very solid framework going forwards.

I only have a few suggestions for improving the manuscript, listed below:

1. The referencing is quite minimal and more relevant references should be cited. An obvious one is Del Signore et al describing KO of OCRL in flies, and there are others on OCRL on endocytosis that were not cited e.g. Erdmann et al, Nandez et al, Choudhury et al.
2. The figure panels should be presented in the right order in the text, which matches their numbering in the figures.
3. Better description is required in a few places in the text so the reader can follow the experiments. For example, what cells are shown in figure 2? How were the PIP probes expressed? Is the imaging in vivo or ex vivo? In Fig 4, how ere the ex vivo experiments performed?
4. The microscopy images in Figure 4 are too dark.
5. Figure S2A needs some sort of schematic so the reader can understand what is being shown.
6. In Fig S2G the PIP2 distribution looks different in the nKO compared to the total KO- more on the PM. Is this a consistent result and what is the explanation if so?
7. In Fig 7 the expression of phosphatase dead OCRL is barely detectable. This makes the functional data difficult to interpret with any certainty. The authors need to be more circumspect in their description of this data and change the writing accordingly.

Significance

The results are clear and convincing and indicate that the Drosophila OCRL KOs (global and nephrocyte-specific) are good models for understanding OCRL function in the kidney. The findings nicely recapitulate what has been shown in human cell lines and previously published zebrafish and mouse models. In that sense the findings are not unexpected and there is some lack of novelty. Nevertheless, the results here, showing the modelling of OCRL in flies, is important to publish. The fly model also offers certain advantages for future studies e.g. ease of genetics and lack of redundancy, which should prove valuable for such investigations. The paper serves as a very solid framework going forwards.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

Seleit and colleagues set out to explore the genetics of developmental timing and tissue size by mapping natural genetic variation associated with segmentation clock period and presomitic mesoderm (PSM) size in different species of Medaka fish. They first establish the extent of variation between five different Medaka species of in terms of organismal size, segmentation rate, segment size and presomitic mesoderm size, among other traits. They find that these traits are species-specific but strongly correlated. In a massive undertaking, they then perform developmental QTL mapping for segmentation clock period and PSM size in a set of ~600 F2 fish resulting from the cross of Orizyas sakaizumii (Kaga) and Orizyas latipes (Cab). Correlation between segmentation period and segment size was lost among the F2s, indicating that distinct genetic modules control these traits. Although the researchers fail to identify causal variants driving these traits, they perform proof of concept perturbations by analyzing F0 Crispants in which candidate genes were knocked out. Overall, the study introduces a completely new methodology (QTL mapping) to the field of segmentation and developmental tempo, and therefore provides multiple valuable insights into the forces driving evolution of these traits.

Major comments: - The first sentence in the abstract reads "How the timing of development is linked to organismal size is a longstanding question". It is therefore disappointing that organismal size is not reported for the F2 hybrids. Was larval length measured in the F2s? If so, it should be reported. It is critical to understand whether the correlation between larval size and segmentation clock period is preserved in F2s or not, therefore determining if they represent a single or separate developmental modules. If larval length data were not collected, the authors need to be more careful with their wording.

The question the reviewer raises here is indeed a very relevant one, and a question that we also were curious about ourselves. While it was not possible (logistically) to grow the 600 F2 fish to adulthood, we did measure larval length in a subset of F2 hatchling (n=72) to ask precisely the question the reviewer raises here. Our results (new Supplementary Figure 5) show that the correlation between larval length and segmentation timing (which we report across the Oryzias species) is absent in the F2s. This indeed argues that the traits represent separate developmental modules.

In the current version of the paper, organismal size is often incorrectly equated to tissue size (e.g. PSM size, segment size). For example, in page 3 lines 33-34, the authors state that faster segmentation occurred in embryos of smaller size (Fig. 1D). However, Fig. 1D shows correlation between segmentation rate and unsegmented PSM area. The appropriate data to show would be segmentation rate vs. larval or adult length.

The reviewer is correct. We have now linked the data more clearly to data we show in Supplementary Figure 1, which shows that adult length and adult mass are strongly correlated (S1A) and that adult mass is in turn strongly correlated with segmentation rate in the different Oryzias species (S1B). Additionally main Figure 1B shows that larval length is correlated with PSM length. We have corrected the main text to reflect these relationships more clearly.

• Is my understanding correct in that the her7-venus reporter is carried by the Cab F0 but not the Kaga F0? Presumably only F2s which carried the reporter were selected for phenotyping. I would expect the location of the reporter in the genome to be obvious in Figure 3J as a region that is only Cab or het but never Kaga. Can the authors please point to the location of the reporter?

The reviewer is correct. Indeed the location of our her7-venus KI is on chromosome 16 and the recombination patterns on this chromosome overwhelmingly show either Hom Cab (green) or Het Cab/Kaga (Black). This is expected as we selected fish carrying the her7-venus KI for phenotyping.

• devQTL mapping in this study seems like a wasted opportunity. The authors perform mapping only to then hand pick their targets based on GO annotations. This biases the study towards genes known to be involved in PSM development, when part of the appeal of QTL mapping is precisely its unbiased nature and the potential to discover new functionally relevant genes. The authors need to better justify their rationale for candidate prioritization from devQTL peaks. The GO analysis should be shown as supplemental data. What criteria were used to select genes based on GO annotations?

We have now commented on these valid points and outlined our rationale in more detail in the text (page 4, lines 20-30). Our rationale now also includes selection of differentially expressed genes (n=5 genes) that fall within segmentation timing devQTL hits (for more details see below). Essentially, while we indeed finally focused on the proof of principle using known genes, these genes were previously not known to play a role in either setting the timing of segmentation or controlling the size of the PSM. Hence, we do think our strategy demonstrates the "the potential to discover new functionally relevant genes", even though the genes themselves had been involved overall in somitogenesis. We added the GO analysis as supplemental data as requested (new Supplementary Figure 7E).

• Analysis of the predicted functional consequence of divergent SNPs (Fig. S6B, F) is superficial. Among missense variants, which genes harbor the most deleterious mutations? Which missense variants are located in highly conserved residues? Which genes carry variants in splice donors/acceptors? Carefully assessing the predicted effect of SNPs in coding regions would provide an alternative, less biased approach to prioritize candidate genes.

We now included our analysis of SNPs based on the Variant effect predictor (VEP) tool from ensembl. This analysis does rank the predicted severity of the SNP on protein structure and function (Impact: low, moderate, high) and does annotate which variants can affect splice donors/acceptors. The VEP analysis for both phenotypes is now added to the manuscript as supplemental data (new Supplementary Data S2, S5).

• Another potential way to prioritize candidate genes within devQTL peaks would be to use the RNA seq data. The authors should perform differential expression analysis between Kaga and Cab RNA-seq datasets. Do any of the differentially expressed genes fall within the devQTL peaks?

As suggested we have performed this additional experiment and report the RNAseq differential analysis in new Supplement Figure 7C-D. The analysis revealed 2606 differentially expressed genes in the PSM between Kaga and Cab, five of which were candidate genes from the devQTL analysis. We now tested all of these (5 in total, 4 new and 1 previously targeted adgrg1) for segmentation timing by CRISPR/Cas9 KO in the her7-venus background, none of which showed a timing phenotype (new Supplementary Figure 7F-F'). We provide the complete set of results in new Supplementary Figure 7 , Supplementary Data file 3 (DE-genes), all data were deposited on publicly available repository Biostudies under accession number: E-MTAB-13927.

• The use of crispants to functionally test candidate genes is inappropriate. Crispants do not mimic the effect of divergent SNPs and therefore completely fail to prove causality. While it is completely understandable that Medaka fish are not amenable to the creation of multiple knock-in lines where divergent SNPs are interconverted between species, better justification is needed. For instance, is there enough data to suggest that the divergent alleles for the candidate genes tested are loss of function? Why was a knockout approach chosen as opposed to overexpression?

We agree with the reviewer that we do not address the causality of SNPs with the CRISPR/Cas9 KO approach we followed. And medaka does offer the genome editing capabilities to create tailored sequence modifications. So in principle, this can be done. In practice, however, we reasoned that any given SNP will contribute only partially to the observed phenotypes and combinatorial sequence edits are simply very laborious given the current state of the art in genome editing technologies. We therefore opted for an alternative proof of principle approach that aims to "to discover new functionally relevant genes", not SNPs.

-Along the same line, now that two candidate genes have been shown to modulate the clock period in crispants (mespb and pcdh10b), the authors should at least attempt to knock in the respective divergent SNPs for one of the genes. This is of course optional because it would imply several months of work, but it would significantly increase the impact of the study.

As above, this is in principle the correct rationale to follow though very time, cost and labour intensive. It is for the later practical consideration that we decided not to follow this option.

Minor Comments - It would be highly beneficial to describe the ecological differences between the two Medaka species. For example, do the northern O. sakaizumii inhabit a colder climate than the southern O. latipes? Is food more abundant or easily accessible for one species compared to the other? What, if anything, has been described about each species' ecology?

There are indeed differences in the ecology of both species, with the northern O.sakaizumii inhabiting a colder climate than the southern O. latipes. In addition, it is known that the breeding season is shorter in the north than the south, and also there is the fact that northern species have been shown to have a faster juvenile growth rate than southern species. While it would be premature to link those ecological factors to the timing differences we observe, we can certainly speculate. A line to this effect has been added to the main text (Page 5, line 28-30).

• The authors describe two different methods for quantifying segmentation clock period (mean vs. intercept). It is still unclear what is the difference between Figs. 3A (clock period), S4A (mean period) and S4B (intercept period). Is clock period just mean period? Are the data then shown twice? How do Fig. 3A and S4A differ?

The clock period shown in all the main figures is the intercept period, which was also used for the devQTL analysis. Both measurements (mean and intercept) are indeed highly correlated and we include both in supplement for completeness.

• devQTL as shorthand for developmental QTL should be defined in page 4 line 1 (where the term first appears), not later in line 12 of the same page.

Noted and corrected, we thank the reviewer for spotting this error.

• Python code for period quantification should be uploaded to Github and shared with reviewers.

All period quantification code that was used in this study was obtained from the publicly available tool Pyboat (https://www.biorxiv.org/content/10.1101/2020.04.29.067744v3). All code that is used in PyBoat is available from the Github page of the creator of the tool (https://github.com/tensionhead/pyBOAT). Both are linked in the references and materials and methods sections.

• RNA-seq data should be uploaded to a publicly accessible repository and the reviewer token shared with reviewers.

We have uploaded all RNA-sequencing Data to public repository BioStudies under accession numbers : E-MTAB-13927, E-MTAB-13928. This information is now also added to material and methods in the manuscript text.

Why are the maintenance (27-28C) vs. imaging (30C) temperatures different?

Medaka fish have a wide range of temperatures they can physiologically tolerate, i.e. 17-33. The temperature 30C was chosen for practical reasons, i.e. a slightly faster developmental rate enables higher sample throughput in overnight real-time imaging experiments.

• For Crispants, control injections should have included a non-targeting sgRNA control instead of simply omitting the sgRNA.

We agree a non-targeting sgRNA control can be included, though we choose a different approach. For clarity, we now also include a control targeting Oca2, a gene involved in the pigmentation of the eye to probe for any injection related effect on timing and PSM size. As expected, 3 sgRNAs + Cas9 against Oca2 had no impact on timing or PSM size. This data is now shown in new Supplementary Figure 9 F-G'.

It is difficult to keep track of the species and strains. It would be most helpful if Fig. S1 appeared instead in main figure 1.

We agree and included an overview of the phylogenetic relationship of all species and their geographical locales in new Figure 1 A-B.

Significance

• The study introduces a new way of thinking about segmentation timing and size scaling by considering natural variation in the context of selection. This new framing will have an important impact on the field.
• Perhaps the most significant finding is that the correlation between segment timing and size in wild populations is driven not by developmental constraints but rather selection pressure, whereas segment size scaling does form a single developmental module. This finding should be of interest to a broad audience and will influence how researchers in the field approach future studies.
• It would be helpful to add to the conclusion the author's opinion on whether segmentation timing is a quantitative trait based on the number of QTL peaks identified.
• The authors should be careful not to assign any causality to the candidate genes that they test in crispants.
• The data and results are generally well-presented, and the research is highly rigorous.
• Please note I do have the expertise to evaluate the statistical/bioinformatic methods used for devQTL mapping.

Reviewer #2

Evidence, reproducibility and clarity

Seleit et al. investigate the correlation between segment size, presomitic mesoderm and the rhythm of periodic oscilations in the segmentation clock of developing medaka fish. Specifically, they aim to identify the genetic determinants for said traits. To do so, they employ a common garden approach and measure such traits in separate strains (F0) and in interbreedings across two generations (F1 and F2). They find that whereas presomitic mesoderm and segment size are genetically coupled, the tempo of her7 oscilations it is not. Genetic mapping of the F0 and F2 progeny allows them to identify regions associated to said traits. They go on an perturb 7 loci associated to the segmentation clock and X related to segment size. They show that 2/7 have a tempo defect, and 2/ affect size.

Major comments: The conclusions are convincing and well supported by the data. I think the work could be published as is in its current state, and no additional experiments that I can think of are needed to support the claims in the paper.

Minor comments: - The authors could provide a more detailed characterization of the identified SNPs associated to the clock and to PSM size. For the segmentation clock, the authors identify 46872 SNPs, most of which correspond to non-coding regions and are associated to 57 genes. They narrow down their approach to those expressed in the PSM of Cab Kaga. Was the RNA selected from F1 hybrids? I wonder if this would impact the analysis for tempo and or size in any way, as F2 are derived from these, and they show broader variability in the clock period than the F0 and F1 fishes.

The RNA was obtained from the pure F0 strains and we have now extended this analysis by deep bulk-RNA sequencing and differential gene expression analysis. As indicated also to reviewer 1, this revealed 2606 differentially expressed genes in the unsegmented tails of Kaga and Cab embryos, some of which occurred in devQTL peaks. Based on this information we expanded our list of CRISPR/Cas9 KOs by targeting all differentially expressed genes (5 in total, 4 new and 1 previously targeted) for segmentation timing, none of which showed a timing phenotype (new Supplementary figure 7C-D). We provide the complete set of results in new Supplementary Figure 7, Supplementary Data file 3 (DE-genes). All data were deposited on publicly available repository Biostudies under accession number: E-MTAB-13927.

It would be good if the authors could discuss if there were any associated categories or overall functional relationships between the SNPs/genes associated to size. And what about in the case of timing?

In the case of PSM size there were no clear GO terms or functional relationships between the genes that passed the significance threshold on chromosome 3.

For the 35 genes related to segmentation timing, there were a number of GO enrichment terms directly related to somitogenesis. We have included the GO analysis in the new Supplementary Figure 7E.

• Have any of the candidate genes or regulatory loci been associated to clock defects (57) or segment size (204) previously in the literature?

To the best of our knowledge none of the genes have been associated with clock or PSM size defects so far. It might be worthwhile using our results to probe their function in other systems enabling higher throughput functional analysis, such as newly developed organoid models.

• When the authors narrow down the candidate list, it is not clear if the genes selected as expressed in the PSM are tissue specific. If they are, I wonder if genes with ubiquitous expression would be more informative to investigate tempo of development more broadly. It would be good if the authors could specifically discuss this point in the manuscript.

We have not addressed the spatial expression pattern of the 35 identified PSM genes in this study, so we cannot speculate further. But the reviewer raises an important point, how timing of individual processes (body axis segmentation) are linked at organismal scale is indeed a fundamental, additional, question that will be addressed in future studies, indeed the in-vivo context we follow here would be ideal for such investigations.

Can the authors speculate mechanistically why mespb or pchd10b accelerates the period of her7 oscillations?

While we do not have a mechanistic explanation yet, an additional experiment we performed, i.e. bulk-RNAsequencing on WT and mespb mutant tails, provided additional insight, we now added this data to the manuscript . This analysis revealed 808 differentially expressed genes between wt and mespb mutants. Interestingly, many of these affected genes are known to be expressed outside of the mespb domain, i.e. in the most posterior PSM (i.e. tbxt, foxb1,msgn1, axin2, fgf8, amongst others). This indicates that the effect of mespb downregulation is widespread and possibly occurs at an earlier developmental stage. This requires more follow up studies. This data is now shown in new Supplementary figure 9A, Supplementary Data file S4. We now comment on this point in the revised manuscript.

• Are there any size difference associated to the functionally validated clock mutants?

We addressed this point directly and added this analysis as supplementary Figure 9H-H'. While pcdh10b mutants do not show any detectable difference in PSM size, we find a small, statistically significant reduction in PSM size (area but not length) in mespb mutants. All this data is now included in the revised manuscript.

-Ref 27 shows a lack of correlation between body size and the segmentation period in various species of mammals. The work supports their findings, and it would be good to see this discussed in the text.

We are not certain how best to compare our in-vivo results in externally developing fish embryos to in-vitro mammalian 2-D cell cultures. In our view, the correlation of embryo size, larval and adult size that we find in Oryzias might not necessarily hold in mammalian species, which would make a comparison more difficult. We do cite the work mentioned so the reader is pointed towards this interesting, complementary literature.

Significance

The work is quite remarkable in terms of the multigenerational genetic analysis performed. The authors have analysed >600 embryos from three separate generations to obtain quantitative data to answer their question (herculean task!). Moreover, they have associated this characterization to specific SNPs. Then, to go beyond the association, they have generated mutant lines and identified specific genes associated to the traits they set out to decipher.

To my knowledge, this is the first project that aims to identify the genetic determinants for developmental timing. Recent work on developmental timing in mammals has focused on interspecies comparisons and does not provide genetic evidence or insight into how tempo is regulated in the genome. As for vertebrates, recent work from zebrafish has profiled temperature effects on cell proportions and developmental timing. However, the genetic approach of this work is quite elegant and neat.

Conceptually, it is quite important and unexpected that overall size and tempo are not related. Body size, lifespan, basal metabolic rates and gestational period correlate positively and we tend to think that mechanistically they would all be connected to one another. This paper and Lazaro et al. 2023 (ref 27) are one of the first in which this preconception is challenged in a very methodical and conclusive manner. I believe the work is a breakthrough for the field and this work would be interesting for the field of biological timing, for the segmentation clock community and more broadly for all developmental biologists.

My field is quantitative stem cell biology and I work on developmental timing myself, so I acknowledge that I am biased in the enthusiasm for the work. It should be noted that as an expert on the field, I have identified instances where other work hasn't been as insightful or well developed in comparison to this piece. It is also worth noting that I am not an expert in fish development, phylogenetic studies or GWAS analyses, so I am not capable to asses any pitfalls in that respect.

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

__Summary: __

This manuscript explores the temporal and spatial regulation of vertebrate body axis development and patterning. In the early stages of vertebrate embryo development, the axial mesoderm (presomitic mesoderm - PSM) undergoes segmentation, forming structures known as somites. The exact genetic regulation governing somite and PSM size, and their relationship to the periodicity of somite formation remains unclear.

To address this, the authors used two evolutionarily closely related Medaka species, Oryzias sakaizumii and Oryzias latipes, which, although having distinct characteristics, can produce viable offspring. Through analysis spanning parental (generation F0) and offspring (generations F1 and F2) generations, the authors observed a correlation between PSM and somite size. However, they found that size scaling does not correlate with the timing of somitogenesis.

Furthermore, employing developmental quantitative trait loci (devQTL) mapping, the authors identified several new candidate loci that may play a role during somitogenesis, influencing timing of segment formation or segment size. The significance of these loci was confirmed through an innovative CRISPR-Cas9 gene editing approach.

This study highlights that the spatial and temporal aspects of vertebrate segmentation are independently controlled by distinct genetic modular mechanisms.

__Major comments: __

1) In the main text page 3, lines 11 and 12, the authors state that the periodicity of the embryo clock of the F1 generation is the intermediate between the parental F0 lineages. However, the authors look only at the periodicity of the Cab strain (Oryzias latipes) segmentation clock. The authors should have a reporter fish line for the Kaga strain (Oryzias sakaizumii) to compare the segmentation clock of both parental strains and their offspring. Since it could be time consuming and laborious, I advise to alternatively rephrase the text of the manuscript.

We agree a careful distinction between segment forming rate (measured based on morphology) and clock period (measured using the novel reporter we generated) is essential. We show that both measures correlate very well in Cab, in both F0 and F1 and F2 carrying the Cab allele. For Kaga F0, we indeed can only provide the rate of somite formation, which nevertheless allows comparison due to the strong correlation to the clock period we have found. We have rephrased the text accordingly.

2) It is evident that only a few F0 and F1 animals were analyzed in comparison with the F2 generation. Could the authors kindly explain whether and how this could bias or skew the observed results?

We provide statistical evidence through the F-test of equality that the variances between the F0, F1 and F2 samples are equal. Additionally if we sub-sample and separate the F2 data into groups of 100 embryos (instead of all 638) we get the same distribution of the F2s. We therefore believe that this is sufficient evidence against a bias or skew in the results.

3) It would be interesting to create fish lines with the validated CRISPR-Cas9 gene manipulations in different genetic contexts (Cab or Kaga) to analyze the true impact on the segmentation clock and/or PSM & somite sizes.

We agree with the reviewer this would in principle be of interest indeed, please see our response to reviewer 1 earlier.

4) Please add the results of the Go Analysis as supplementary material.

We have added the GO analysis in new Supplementary Figure 7E.

__Minor comments: __

1) In the main text, page 2, line 29, Supplementary Figure 1D should be referenced.

We have added a clearer phylogeny and geographical location of the different species in new Figure 1 A-B. And reference it at the requested location.

2) In the main text, page 2, line 32, the authors refer to Figure 1B, but it should be 1C.

We have corrected the information.

3) Regarding the topic "Correlation of segmentation timing and size in the Oryzias genus" the authors should also give information on the total time of development of the different Oryzias species, as well as the total number of formed somites.

We follow this recommendation and have added this information in new Supplementary Figure 5. We also now include segment number measured in F2 embryos. We indeed view segmentation rate as a proxy for developmental rate, which however needs to be distinguished from total developmental time. The latter can be measured for instance by quantifying hatching time, which we did. These measurements show that Kaga, Cab and O.hubbsi embryos kept at constant 28 degrees started hatching on the same day while O.minutillus and O.mekongensis embryos started hatching one day earlier. We have not included this data in the manuscript because we think a distinction should be made between rate of development and total development time.

4) In Figures 3A and B, please add info on the F1 lines for comparison.

The information on F1 lines is provided in Supplementary Figure 3

5) Supplementary Figures 2F shows that the generation F1 PSM is similar to Cab F0, and not an intermediate between Kaga F0 and Cab F0. This is interesting and should be discussed.

We show that the F1 PSM is indeed closer to the PSM of Cab than it is to the Kaga PSM. This is indeed intriguing and we have now commented on this point directly in the text.

6) Supplementary Figures 6C to H are not mentioned either in the main text or in the extended information. Please add/mention accordingly.

We have added references to both in the text

7) The order of Supplementary Figure 8 E to H and A to D appears to be not correct and not following the flow of the text. Please update/correct accordingly.

We have updated the text accordingly.

8) The authors should choose between "Fig.", "Fig", "fig.", "fig" or "Figure". All 'variants' can be found in the text.

Noted, and updated. Fig. is used for main figures and fig. is used for supplementary figures.

9) The color scheme of several figures (graphs with colored dots) should be revised. Several appear to be difficult to discern and analyze.

We have enhanced the colours and increased the font on the figure panels. The colour panel was chosen to be colour-blind friendly.

10) Please address/discuss following questions: What are the known somitogenesis regulating genes in Medaka? How do they correlate with the new candidates?

The candidates we found and tested had not been implicated in regulating the tempo of segmentation or PSM size, while for some a role in somite formation had been previously established, hence the enrichment in GO analysis Somitogenesis.

Reviewer #3 (Significance (Required)):

General assessment:

This interesting manuscript describes a novel approach to study and find new players relevant to the regulation of vertebrate segmentation. By employing this innovative methodology, the authors could elegantly demonstrate that the segmentation clock periodicity is independent from the sizes of the PSM and forming somites. The authors were further able to find new genes that may be involved in the regulation of the segmentation clock periodicity and/or the size of the PSM & somites. A limitation of this study is the fact that the results mainly rely on differences between the two species. The integration of additional Medaka species would be beneficial and may help uncover relevant genes and genetic contexts.

Advance:

To my best knowledge this is the first time that such a methodology was employed to study the segmentation clock and axial development. Although the topic has been extensively studied in several model organisms, such as mice, chicken, and zebrafish, none of them correlated the size of the embryonic tissues and the periodicity of the embryo clock. This study brings novel technological and functional advances to the study of vertebrate axial development.

Audience:

This work is particularly interesting to basic researchers, especially in the field of developmental biology and represents a fresh new approach to study a core developmental process. This study further opens the exciting possibility of using a similar methodology to investigate other aspects of vertebrate development. It is a timely and important manuscript which could be of interest to a wider scientific audience and readership.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This manuscript explores the temporal and spatial regulation of vertebrate body axis development and patterning. In the early stages of vertebrate embryo development, the axial mesoderm (presomitic mesoderm - PSM) undergoes segmentation, forming structures known as somites. The exact genetic regulation governing somite and PSM size, and their relationship to the periodicity of somite formation remains unclear.

To address this, the authors used two evolutionarily closely related Medaka species, Oryzias sakaizumii and Oryzias latipes, which, although having distinct characteristics, can produce viable offspring. Through analysis spanning parental (generation F0) and offspring (generations F1 and F2) generations, the authors observed a correlation between PSM and somite size. However, they found that size scaling does not correlate with the timing of somitogenesis.

Furthermore, employing developmental quantitative trait loci (devQTL) mapping, the authors identified several new candidate loci that may play a role during somitogenesis, influencing timing of segment formation or segment size. The significance of these loci was confirmed through an innovative CRISPR-Cas9 gene editing approach.

This study highlights that the spatial and temporal aspects of vertebrate segmentation are independently controlled by distinct genetic modular mechanisms.

Major comments:

1. In the main text page 3, lines 11 and 12, the authors state that the periodicity of the embryo clock of the F1 generation is the intermediate between the parental F0 lineages. However, the authors look only at the periodicity of the Cab strain (Oryzias latipes) segmentation clock. The authors should have a reporter fish line for the Kaga strain (Oryzias sakaizumii) to compare the segmentation clock of both parental strains and their offspring. Since it could be time consuming and laborious, I advise to alternatively rephrase the text of the manuscript.
2. It is evident that only a few F0 and F1 animals were analyzed in comparison with the F2 generation. Could the authors kindly explain whether and how this could bias or skew the observed results?
3. It would be interesting to create fish lines with the validated CRISPR-Cas9 gene manipulations in different genetic contexts (Cab or Kaga) to analyze the true impact on the segmentation clock and/or PSM & somite sizes.
4. Please add the results of the Go Analysis as supplementary material.

Minor comments:

1. In the main text, page 2, line 29, Supplementary Figure 1D should be referenced.
2. In the main text, page 2, line 32, the authors refer to Figure 1B, but it should be 1C.
3. Regarding the topic "Correlation of segmentation timing and size in the Oryzias genus" the authors should also give information on the total time of development of the different Oryzias species, as well as the total number of formed somites.
4. In Figures 3A and B, please add info on the F1 lines for comparison.
5. Supplementary Figures 2F shows that the generation F1 PSM is similar to Cab F0, and not an intermediate between Kaga F0 and Cab F0. This is interesting and should be discussed.
6. Supplementary Figures 6C to H are not mentioned either in the main text or in the extended information. Please add/mention accordingly.
7. The order of Supplementary Figure 8 E to H and A to D appears to be not correct and not following the flow of the text. Please update/correct accordingly.
8. The authors should choose between "Fig.", "Fig", "fig.", "fig" or "Figure". All 'variants' can be found in the text.
9. The color scheme of several figures (graphs with colored dots) should be revised. Several appear to be difficult to discern and analyze.
10. Please address/discuss following questions: What are the known somitogenesis regulating genes in Medaka? How do they correlate with the new candidates?

Significance

General assessment:

This interesting manuscript describes a novel approach to study and find new players relevant to the regulation of vertebrate segmentation. By employing this innovative methodology, the authors could elegantly demonstrate that the segmentation clock periodicity is independent from the sizes of the PSM and forming somites. The authors were further able to find new genes that may be involved in the regulation of the segmentation clock periodicity and/or the size of the PSM & somites. A limitation of this study is the fact that the results mainly rely on differences between the two species. The integration of additional Medaka species would be beneficial and may help uncover relevant genes and genetic contexts.

Advance:

To my best knowledge this is the first time that such a methodology was employed to study the segmentation clock and axial development. Although the topic has been extensively studied in several model organisms, such as mice, chicken, and zebrafish, none of them correlated the size of the embryonic tissues and the periodicity of the embryo clock. This study brings novel technological and functional advances to the study of vertebrate axial development.

Audience:

This work is particularly interesting to basic researchers, especially in the field of developmental biology and represents a fresh new approach to study a core developmental process. This study further opens the exciting possibility of using a similar methodology to investigate other aspects of vertebrate development. It is a timely and important manuscript which could be of interest to a wider scientific audience and readership.

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

Seleit et al. investigate the correlation between segment size, presomitic mesoderm and the rhythm of periodic oscilations in the segmentation clock of developing medaka fish. Specifically, they aim to identify the genetic determinants for said traits. To do so, they employ a common garden approach and measure such traits in separate strains (F0) and in interbreedings across two generations (F1 and F2). They find that whereas presomitic mesoderm and segment size are genetically coupled, the tempo of her7 oscilations it is not. Genetic mapping of the F0 and F2 progeny allows them to identify regions associated to said traits. They go on an perturb 7 loci associated to the segmentation clock and X related to segment size. They show that 2/7 have a tempo defect, and 2/ affect size.

Major comments:

The conclusions are convincing and well supported by the data. I think the work could be published as is in its current state, and no additional experiments that I can think of are needed to support the claims in the paper.

Minor comments:

• The authors could provide a more detailed characterization of the identified SNPs associated to the clock and to PSM size. For the segmentation clock, the authors identify 46872 SNPs, most of which correspond to non-coding regions and are associated to 57 genes. They narrow down their approach to those expressed in the PSM of Cab Kaga. Was the RNA selected from F1 hybrids? I wonder if this would impact the analysis for tempo and or size in any way, as F2 are derived from these, and they show broader variability in the clock period than the F0 and F1 fishes.

• It would be good if the authors could discuss if there were any associated categories or overall functional relationships between the SNPs/genes associated to size. And what about in the case of timing?

• Have any of the candidate genes or regulatory loci been associated to clock defects (57) or segment size (204) previously in the literature?

• When the authors narrow down the candidate list, it is not clear if the genes selected as expressed in the PSM are tissue specific. If they are, I wonder if genes with ubiquitous expression would be more informative to investigate tempo of development more broadly. It would be good if the authors could specifically discuss this point in the manuscript.

• Can the authors speculate mechanistically why mespb or pchd10b accelerates the period of her7 oscillations?

• Are there any size difference associated to the functionally validated clock mutants?

• Ref 27 shows a lack of correlation between body size and the segmentation period in various species of mammals. The work supports their findings, and it would be good to see this discussed in the text.

Significance

The work is quite remarkable in terms of the multigenerational genetic analysis performed. The authors have analysed >600 embryos from three separate generations to obtain quantitative data to answer their question (herculean task!). Moreover, they have associated this characterization to specific SNPs. Then, to go beyond the association, they have generated mutant lines and identified specific genes associated to the traits they set out to decipher.

To my knowledge, this is the first project that aims to identify the genetic determinants for developmental timing. Recent work on developmental timing in mammals has focused on interspecies comparisons and does not provide genetic evidence or insight into how tempo is regulated in the genome. As for vertebrates, recent work from zebrafish has profiled temperature effects on cell proportions and developmental timing. However, the genetic approach of this work is quite elegant and neat.

Conceptually, it is quite important and unexpected that overall size and tempo are not related. Body size, lifespan, basal metabolic rates and gestational period correlate positively and we tend to think that mechanistically they would all be connected to one another. This paper and Lazaro et al. 2023 (ref 27) are one of the first in which this preconception is challenged in a very methodical and conclusive manner. I believe the work is a breakthrough for the field and this work would be interesting for the field of biological timing, for the segmentation clock community and more broadly for all developmental biologists.

My field is quantitative stem cell biology and I work on developmental timing myself, so I acknowledge that I am biased in the enthusiasm for the work. It should be noted that as an expert on the field, I have identified instances where other work hasn't been as insightful or well developed in comparison to this piece. It is also worth noting that I am not an expert in fish development, phylogenetic studies or GWAS analyses, so I am not capable to asses any pitfalls in that respect.

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

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Referee #1

Evidence, reproducibility and clarity

Seleit and colleagues set out to explore the genetics of developmental timing and tissue size by mapping natural genetic variation associated with segmentation clock period and presomitic mesoderm (PSM) size in different species of Medaka fish. They first establish the extent of variation between five different Medaka species of in terms of organismal size, segmentation rate, segment size and presomitic mesoderm size, among other traits. They find that these traits are species-specific but strongly correlated. In a massive undertaking, they then perform developmental QTL mapping for segmentation clock period and PSM size in a set of ~600 F2 fish resulting from the cross of Orizyas sakaizumii (Kaga) and Orizyas latipes (Cab). Correlation between segmentation period and segment size was lost among the F2s, indicating that distinct genetic modules control these traits. Although the researchers fail to identify causal variants driving these traits, they perform proof of concept perturbations by analyzing F0 Crispants in which candidate genes were knocked out. Overall, the study introduces a completely new methodology (QTL mapping) to the field of segmentation and developmental tempo, and therefore provides multiple valuable insights into the forces driving evolution of these traits.

Major comments:

• The first sentence in the abstract reads "How the timing of development is linked to organismal size is a longstanding question". It is therefore disappointing that organismal size is not reported for the F2 hybrids. Was larval length measured in the F2s? If so, it should be reported. It is critical to understand whether the correlation between larval size and segmentation clock period is preserved in F2s or not, therefore determining if they represent a single or separate developmental modules. If larval length data were not collected, the authors need to be more careful with their wording. In the current version of the paper, organismal size is often incorrectly equated to tissue size (e.g. PSM size, segment size). For example, in page 3 lines 33-34, the authors state that faster segmentation occurred in embryos of smaller size (Fig. 1D). However, Fig. 1D shows correlation between segmentation rate and unsegmented PSM area. The appropriate data to show would be segmentation rate vs. larval or adult length.
• Is my understanding correct in that the her7-venus reporter is carried by the Cab F0 but not the Kaga F0? Presumably only F2s which carried the reporter were selected for phenotyping. I would expect the location of the reporter in the genome to be obvious in Figure 3J as a region that is only Cab or het but never Kaga. Can the authors please point to the location of the reporter?
• devQTL mapping in this study seems like a wasted opportunity. The authors perform mapping only to then hand pick their targets based on GO annotations. This biases the study towards genes known to be involved in PSM development, when part of the appeal of QTL mapping is precisely its unbiased nature and the potential to discover new functionally relevant genes. The authors need to better justify their rationale for candidate prioritization from devQTL peaks. The GO analysis should be shown as supplemental data. What criteria were used to select genes based on GO annotations?
• Analysis of the predicted functional consequence of divergent SNPs (Fig. S6B, F) is superficial. Among missense variants, which genes harbor the most deleterious mutations? Which missense variants are located in highly conserved residues? Which genes carry variants in splice donors/acceptors? Carefully assessing the predicted effect of SNPs in coding regions would provide an alternative, less biased approach to prioritize candidate genes.
• Another potential way to prioritize candidate genes within devQTL peaks would be to use the RNA seq data. The authors should perform differential expression analysis between Kaga and Cab RNA-seq datasets. Do any of the differentially expressed genes fall within the devQTL peaks?
• The use of crispants to functionally test candidate genes is inappropriate. Crispants do not mimic the effect of divergent SNPs and therefore completely fail to prove causality. While it is completely understandable that Medaka fish are not amenable to the creation of multiple knock-in lines where divergent SNPs are interconverted between species, better justification is needed. For instance, is there enough data to suggest that the divergent alleles for the candidate genes tested are loss of function? Why was a knockout approach chosen as opposed to overexpression?
• Along the same line, now that two candidate genes have been shown to modulate the clock period in crispants (mespb and pcdh10b), the authors should at least attempt to knock in the respective divergent SNPs for one of the genes. This is of course optional because it would imply several months of work, but it would significantly increase the impact of the study.

Minor Comments

• It would be highly beneficial to describe the ecological differences between the two Medaka species. For example, do the northern O. sakaizumii inhabit a colder climate than the southern O. latipes? Is food more abundant or easily accessible for one species compared to the other? What, if anything, has been described about each species' ecology?
• The authors describe two different methods for quantifying segmentation clock period (mean vs. intercept). It is still unclear what is the difference between Figs. 3A (clock period), S4A (mean period) and S4B (intercept period). Is clock period just mean period? Are the data then shown twice? How do Fig. 3A and S4A differ?
• devQTL as shorthand for developmental QTL should be defined in page 4 line 1 (where the term first appears), not later in line 12 of the same page.
• Python code for period quantification should be uploaded to Github and shared with reviewers.
• RNA-seq data should be uploaded to a publicly accessible repository and the reviewer token shared with reviewers.
• Why are the maintenance (27-28C) vs. imaging (30C) temperatures different?
• For Crispants, control injections should have included a non-targeting sgRNA control instead of simply omitting the sgRNA.
• It is difficult to keep track of the species and strains. It would be most helpful if Fig. S1 appeared instead in main figure 1.

Significance

• The study introduces a new way of thinking about segmentation timing and size scaling by considering natural variation in the context of selection. This new framing will have an important impact on the field.
• Perhaps the most significant finding is that the correlation between segment timing and size in wild populations is driven not by developmental constraints but rather selection pressure, whereas segment size scaling does form a single developmental module. This finding should be of interest to a broad audience and will influence how researchers in the field approach future studies.
• It would be helpful to add to the conclusion the author's opinion on whether segmentation timing is a quantitative trait based on the number of QTL peaks identified.
• The authors should be careful not to assign any causality to the candidate genes that they test in crispants.
• The data and results are generally well-presented, and the research is highly rigorous.
• Please note I do have the expertise to evaluate the statistical/bioinformatic methods used for devQTL mapping.

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Reply to the reviewers

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

Summary:* In this paper the authors explore the function of Syndecan in Drosophila stem cells focussing primarily on the intestinal stem cells. They use RNAi knockdown to conclude that Syndecan is required for long term stem cell maintenance as its knockdown results in apoptosis. They suggest that this effect is independent of LINC complex proteins but is associated with changes to nuclear morphology and DNA damage. They go on to show that a similar impact on nuclear shape can be seen in larval neuroblasts but not in stem cells of the female germline. *

Major Comments: *The key conclusion that underpins the paper is that reduced Syndecan causes loss of stem cells. This is based entirely on evidence from cell-type specific RNAi using 3 independent RNAi lines. Overexpression has no phenotype and there is no analysis of loss of function mutants. SdcRNAi3 gives strong phenotypes that are statistically significant and is used throughout the paper. SdcRNAi2 gives comparatively moderate phenotypes which trend in the same direction but it is not clear if these are statistically significant (Fig S1). SdcRNAi line 1 appears to have very little effect (and if anything trends in the opposite direction in S1A). In addition, the knockdown efficiency of the three lines has not been assessed. Another possible concern given the dependence on RNAi3 is that the RNAi control line used is not an ideal match for the VDRC GD RNAi lines as it is in a different genetic background. In order to robustly draw conclusions: the phenotypes with RNAi lines 1 and 2 should be tested for significance; the extent of knockdown in each should be quantified either by qPCR in whole tissue knockdown, or by staining for protein levels if possible, to assess whether the variation in phenotypes is due to different knockdown levels. The use of a loss of function mutant in clones or tissue specific CRISPR-Cas9 KO or KD would also significantly increase confidence in the findings. *

• Our qPCR data indicate that SdcRNAi3 produces the most efficient knockdown, whilst SdcRNAi1 generates the weakest knockdown. The new manuscript version will incorporate this data in figure S1. Knockdown efficacy of SdcRNAi 3 has also been previously reported (Eveland et al., 2016).

• We apologise for omitting to add the statistical tests on phenotypic categories in figure S1A, this will be revised. We confirm that all Sdc RNAi phenotypic distributions are significantly different to that seen for age-matched controls (p- It should also be noted that despite weaker knockdowns with SdcRNAi1 and 2, we still observed statistically significant ISC depletion after 28 days of RNAi expression - we will add this data in figure S1. Overall, we are confident about Sdc’s role in maintaining intestinal stem cells.

*Similarly, the evidence for a lack of LINC protein role in the phenotype relies on single RNAi lines without validation of knockdowns. The authors should ideally validate these lines in this system or reference other studies that have validated the lines in this or other contexts. *

• The klarsicht RNAi line (BDSC 36721) and klaroid RNAi line (BDSC 40924) used in this study have been validated and used in other studies. (Falo-Sanjuan & Bray, 2022; Collins et al., 2017)

• For Msp300 RNAi knockdown we have used two independent RNAi lines which gave similar results. We will amend the text to clarify these points. In addition, the line reported in the manuscript was previously validated (Dondi et al., 2021; Frost et al., 2016).

Minor Comments: *The figures are generally very clear but some of the IF image panels are very small and require significant on-screen enlargement to be legible. In particular in Figure 1B the cross section views make it difficult to assess expression in the different cell types (and don't show very many cells), could this be shown in wholemount or as separated channels in a supplementary figure? In addition, it would strengthen the argument to include counterstains for markers of the different cell types (particularly to distinguish ISC/EB from EE). This could include esg-lacZ to mark ISC/EBs or prospero for EEs. However, if a broader view of these panels makes it clearer that all epithelial cells are expressing Syndecan this may not be essential. *

• We are happy to incorporate larger fields of view, and co-immunostaining with different cell type markers.

*Syndecan is referred to throughout as a stem cell regulator. This implies that in certain contexts or in response to certain stimuli its expression may be altered to elicit a stem cell response but no examples of this are shown. Moreover, only knockdown and not overexpression gives phenotypes suggesting its role may be as a required protein than a regulator. Either examples of its expression being modulated in homeostasis or in response to a challenge could be included or the wording could be amended. *

• We agree with the reviewer and will amend the wording.

*Expression of Syndecan in neuroblasts is described as data not shown, it would be better to include this for completeness. *

• We will add this data in figure 4.

*In addition to the intestinal validation of the Syndecan RNAi lines, validation of knockdown in the germline would be valuable to support the conclusions of Fig S4 given differences of knockdown in the germline with some RNAi lines (although inclusion of Dicer in the driver line should have overcome this). *

• Sdc expression is very low in the germline, compared to the surrounding somatic cells, therefore we are not confident that we can detect differences in expression level after knockdown. We suggest adding a panel in figure S4 to show the low expression and adding a comment in the text. Reviewer #1 (Significance (Required)): *The study describes a potentially very interesting, novel link between Syndecan, nuclear shape and apoptosis in cycling cells that could have broad relevance. If fully validated this could have implications for other stem cell populations, including those in mammals and disease relevance in the context of cancer. The paper is fundamentally descriptive in nature and so the level of significance hinges on the strength of evidence and how interesting the phenotype itself is. At this stage the audience will be primarily in the areas of fundamental research in biology of the nucleus and cytoskeleton. Defining the mechanistic link between Syndecan and nuclear morphology will be a critical next step and while not essential for this study would significantly increase the likely interest in the paper. *

• We thank the reviewer for these constructive comments. We agree that discovering the mechanistic links between Syndecan and nuclear morphology in future studies, in this and other model systems, will be relevant to many areas of biological research.

*In terms of significance in stem cell biology the distinction between a regulator and a requirement to prevent stem cell apoptosis is important and the lack of evidence for a context in which Syndecan plays a regulatory role somewhat detracts from the breadth of impact. My field of expertise is in epithelial stem cell biology. *

• We agree and will amend our wording.

Reviewer #2 *(Evidence, reproducibility and clarity (Required)): ** Summary: Stem cell (SC) maintenance and proliferation are necessary for tissue morphogenesis and homeostasis. The basement membrane (BM) has been shown to play a key role in regulating stem cell behavior. In this work, the authors unravel a new connection between the receptor for BM components Syndecan (Sdc) and SC behavior, using Drosophila as model system. They show that Sdc is required for intestine stem cell (ISC) maintenance, as Sdc depletion results in their progressive loss. At a cellular level, they also find that Sdc depletion in ISCs affects cell survival, cell and nuclear shape, nuclear lamina and DNA damage. In addition, they show that the defects in shape are not related to cell death. They also find that Sdc depletion in neural stem cells also results in nuclear envelope remodeling during cell division. This is in contrast to what happens in female germline stem cells where Sdc does not seem to be required for their survival or maintenance. In general, I believe that this work unravels a connection between Sdc and stem cell behavior. However, I think the study is still at a preliminary stage, as how Sdc regulates different facets of stem cell behavior remains unclear.

Major comments: 1. To clearly show that the cellular changes produced by loss of Sdc are not due to cell death, one should quantify the ISC area and shape of Sdc-depleted ISCs expressing DIAP1 and compare it to that of Sdc-depleted ISCs. As DIAP1 overexpression only partially rescues ISC loss due to Sdc depletion, one should show that the Sdc-depleted ISCs expressing DIAP1 that still show cellular changes are not dying, as overexpression of Diap1 might not be sufficient to completely rescue cell death in all Sdc-depleted ISCs. In fact, apoptosis in Sdc depleted guts and the ability of Diap1 overexpression to rescue cell death should be analyzed using markers of caspase activity, this will provide a better idea of the contribution of apoptosis to the phenotypes associated to Sdc depletion. *

• We can, as suggested by the reviewer, quantify the area and shape of Sdc-depleted ISCs expressing DIAP1 and compare it to that of Sdc-depleted ISCs. However, our immunostainings with anti-Caspase 3 or Drice do not pick up apoptotic cells in the fly gut. This is not entirely unexpected, as apoptosis is unfortunately not easily detected in this tissue. In the absence of a positive readout of apoptosis, we will not be able to discriminate between apoptotic and non-apoptotic stem cells when quantifying area and shape and will only have global quantifications.

• The authors show that ISC loss is associated with reduced cell density, suggesting that this is most likely due to failure in new cell production. What do they mean with cell production? Is this related to a problem in regulating cell division or to the fact that as some ISCs are lost by apoptosis there is progressively less ISCs or to a combination of both? I think that cell division should be monitored throughout time as well as cell death in ISCs.*

• Based on esgF/O experiments (fig. 1D-F and S1C) where we can trace the production of new cells with GFP, we know that Sdc RNAi expression (i) impairs the appearance of newly differentiated cells in the tissue and (ii) results in the disappearance of progenitor cells (fig. S1C). Supporting these points, (i) we have observed PH3+ mitotic stem cells upon Sdc RNAi, so we are confident the cells are able to initiate cell division (see also fig. 2G), and (ii) we have occasionally noted in fixed samples stem cells looking like they were in the process of delaminating. Overall, the failure of cell production is likely related to problems with both completion of cell division and progressive stem cell loss. High resolution live imaging will in future give us a better insight into stem cell division dynamics/behaviour, however, the technical improvements required are beyond the scope of this project. In the meantime, we propose to clarify our statement in the text.

• The authors report that in contrast to what happens when Sdc is eliminated from ISCs, its elimination from EEs results in an increase in the number of these cells. An explanation for this result is missing.*

• Based on known roles of Syndecan in other Drosophila tissues (Johnson et al., 2004; Steigemann et al., 2004; Chanana et al., 2009; Schulz et al., 2011), we speculate that Syndecan may contribute to robo/slit signalling, which is an important regulator of EE activity in the Drosophila gut (Biteau & Jasper 2014; Zeng et al., 2015). We propose to amend the text to express this hypothesis.

• The authors suggest that "Sdc function is unlikely to be fully accounted for by individual LINC complex proteins, although these proteins might act redundantly". Checking redundancy seems a straight forward experiment, which only requires the simultaneous expression of RNAis against several of these proteins. This would help to settle the implication of LINC complex proteins on Sdc function.*

• To check redundancy, we propose to combine Klaroid RNAi with Msp300 or Klarsicht RNAis, and express two RNAis at a time in ISCs. We will then measure stem cell proportions and the proportion of ISCs with DNA damage.

• Although quantification of DNA damage, by immunolabelling with gH2Av, reveals that knockdown of individual LINC complex components did not recapitulate the damage observed upon Sdc depletion (Fig.3G), the image shown in Fig.3F reflects much higher levels of gH2Av in Msp300 RNAi cells compared to Sdc RNAi cells. Authors should clarify this. *

• Like the reviewer, we are intrigued by the higher levels of H2Av staining in the tissue, despite Msp300 knockdown in stem cells only (fig. 3F). It is worth noting that we observed this with two independent RNAi lines (we showed only one RNAi in the manuscript, but we will amend the text to indicate this). In fig. 3F, we will indicate with an arrow the only ISC that is H2Av positive, and mention in the text that the majority of DNA damage signal observed in the Msp300 RNAi condition is in enterocytes, not ISCs. We currently do not have an explanation for why loss of Msp300 in ISCs should cause DNA damage in neighboring cells.

*In addition, the consequences of the simultaneous elimination of more than one component of the LINC complex on DNA damage should be analyzed. *

• We agree, and as we check for redundancy (as in point 4), we will also immunostain the tissues for H2Av.

• The authors claim that the fact that "DNA damage was found more frequently in Sdc-depleted ISCs with lamina invaginations compared to those without (Figure 3H), supports a model whereby the development of nuclear lamina invaginations precedes the acquisition of DNA damage". However, to me, these results show that there is a relation between these two phenotypes, but not that one precedes the other. In order to show which one is the possible cause and which the consequence, the authors should perform a time course of the appearance of each of these phenotypes.*

• We agree with the reviewer that we should rephrase our statement to indicate a relationship between lamina invaginations and DNA damage, rather than a causality (as stated in fig. 3H).

(In terms of performing a time course analysis, the difficulty is that after 3 days of Sdc RNAi expression, the apparent DNA damage (fig. 3G) corresponds to a very small proportion of stem cells, meaning that an exceptionally large sample size would be required to achieve robust statistical analysis.)

• When studying the role of Sdc in neural stem cells, the authors show that elimination of Sdc in neuroblasts also affect nuclear envelope and shape. Furthermore, in this case, they also show that Sdc elimination affects cell division. To look for a more conserved role of Sdc in stem cell behavior, I believe the authors should also analyze whether Sdc elimination in neural stem cells results in an increase in DNA damage, as it is the case in ISCs.*

• We will stain larval brains for H2Av to see if DNA damage is also observed following Sdc knockdown in neuroblasts.

• When analyzing a possible role of Sdc in fGSCs, quantification of germline stem cells and gH2Av levels in control nosGal4 and nos>Sdc RNAi germaria should be done. In addition, it is not clear to me whether Sdc is in fact expressed in fGSCs.*

• *

• As mentioned in comments to reviewer 1, we will add a panel in figure S4 to show the low Sdc expression in fGSCs. We will also clarify in the text that we do not see any H2Av staining in the fGSCs (thus, there is nothing to quantify in this case).

* The authors should show presence of Sdc in neuroblasts.*

• Yes, we agree, as also mentioned in comments to reviewer 1.

Reviewer #2 (Significance (Required)): *In general, although this work reveals that elimination of Sdc affects different aspects of intestinal and neural stem cell behavior, including cell survival, cell production, nuclear shape, nuclear lamina or DNA damage, their contribution to stem cell loss and interactions between them have not been analyzed in detail. The role of the basement membrane in stem cell behavior has been extensively studied. In particular, the role of syndecan in stem cell regulation has been primarily confined to cancer, muscle, neural and hematopoietic stem cells. Thus, the study here presented could extend the role of Sdc to intestinal stem cells and could potentially reveals a conserved role for Sdc in neural stem cell behavior. However, the problem with the data mentioned above, hinders the assessment of the significance of this work. *

• We thank the reviewer for their assessment and are glad that they also find that our study provides novel connections between Syndecan and the regulation of intestinal and neural stem cell behaviors. To strengthen our conclusions, we will include additional experiments or amend the text, as indicated above.

Reviewer #3* (Evidence, reproducibility and clarity (Required)): ** Peer-review: The transmembrane protein Syndecan regulates stem cell nuclear properties and cell maintenance.

In this work, the authors investigate the role of the transmembrane protein Syndecan (Sdc) in nuclear organisation and stem cell maintenance. Theys show that Sdc knockdown in intestinal stem cells (ISCs) results in a reduction of the ISC pool as well as of their progeny. They hypothesise that these ISCs might get eliminated via cell death, however, expression of the apoptotic inhibitor DIAP1 only rescued ISC loss by 50%. Hence, they suggest that apoptosis can not account for the total decrease in ISCs observed upon Sdc loss. ISCs depleted from Sdc exhibited abnormal cytoplasmic and nuclear morphologies. As Sdc has previously been implicated in the abscission machinery in mammalian cultured cells, they tested if Sdc could be playing a similar role in the abscission of ISCs. However, ISCs were capable of undergoing cytokinesis. Next, they tested if Sdc depletion could be altering the linkage between the plasma membrane and the nucleus mediated by the Linker of Nucleoskeleton and Cytoskeleton (LINC) complex. However, individual knockdowns of the different components of the complex did not disrupt the nuclear morphology to the same extent as Sdc knockdown, suggesting that Sdc function may be independent of the LINC complex. Finally, they observed that Sdc-depleted ISCs exhibited DNA damage, suggesting that Sdc may play a role in DNA protection. The authors next tested if Sdc played similar roles in other stem cell types such as the female germline stem cells (fGSCs) and larval neural stem cells (NSCs). While Sdc depletion appeared dispensable for fGSC maintenance, it prolonged NSC divisions and altered the nuclear morphology of NSCs. Upon further investigations, they observed that the NSC's nuclear envelope was disrupted upon division, hence causing defects in the nuclear size ratio of NSC and their progeny. This study provides with interesting findings in the field and proves a new role for Sdc in the regulation of intestinal and neural stem cell maintenance. I would recommend this manuscript to be accepted if the authors address the following comments.

__Major comments: __ 1. In Figure 2 A-B, Sdc RNAi should ideally have a UAS control transgene to match the number of UAS being expressed to that of Sdc RNAi, DIAP1. Otherwise, it is plausible that reduced RNAi expression of Sdc RNAi, DIAP1 animals is the cause of the partial rescue. Staining against cell death markers such as Dcp-1 or TUNEL might also quantify the number of cells undergoing cell death in each of the genotypes. *

• As mentioned in comments to reviewer 2 (point 1), it is difficult to label apoptotic cells in the fly gut. However, we could set up an additional control to test that the partial rescue observed upon DIAP1 expression is not a result of Gal4 dilution.

• " These phenotypes were observed both with and without DIAP1 expression (Figure 2C), indicating that these cell shapes are not caused by apoptosis."Misleading, as DIAP overexpression in Sdc knockdown background only rescued apoptosis by 50%. Hence, it is possible that those cells undergoing morphological defects, protrusions and blebbing might still undergo death - also considering those morphological changes are typically observed in apoptotic cells...Therefore, to rule apoptosis out, these cells should be shown to be negative for cell death markers. *

• We agree, however, it is difficult to label apoptotic cells. We think that the quantification of shape and area (as suggested by reviewer 2, point 1) will clearly show that the cell shapes resulting from Sdc depletion are not caused by apoptosis.

• Show if Sdc is expressed in fGSCs - the lack of phenotype caused by Sdc knockdown might be due to lack of expression of Sdc.*

• As mentioned in comments to reviewers 1&2, we will add a panel in figure S4 to show the low sdc expression in fGSCs.

• "After confirming the presence of Sdc in neuroblasts (data not shown)."Data should be shown. It would be of great interest for researchers if you showed a staining of different brain cell types (NBs, glia, neurons) and the Sdc expression patterns.*

• As mentioned in comments to reviewers 1&2, we will add a panel in figure 4 to show sdc expression in NBs and the overall expression pattern.

• You show how Slc-depleted NBs have disrupted nuclear morphologies. However, does Slc KD in NB lineages affect their ability to self-renew and generate differentiated progeny? Is the number of NBs and of their progeny cells altered as it is for ISCs?*

• We propose to knockdown Sdc in NBs and quantify brain size in 3rd instar larvae to test if the ability to generate progeny is affected.

• Does protection against DNA damage in an Slc knockdown background prevent the defects observed with the single knockdown and ISC elimination?*

• This is a good question, and we should emphasize this point in the discussion. However, because of the multiple routes of DNA damage response, and the multiple lines needed to explore this connection, we feel that investigating this question is beyond this project.

• Any idea the similarities between ISC and NBs that can account for why Sdc knockdown has effects in those systems, while no effect was observed in the germ cells?*

• Besides the differences in expression level, we speculate that GSCs may have a different nuclear / lamina architecture which might reflect differences in how GSCs control the physical integrity of their nuclei. It is also possible that the differences observed between tissues reflect the way stem cells connect to their microenvironment. Notably, fGSCs rely extensively on E-Cadherin mediated adhesion with neighbouring cells, and it is possible that contact with the extracellular matrix is dispensable. We will consider these possibilities in the discussion.

Minor comments:* ** 8. Lamina invaginations, for example in Figure 3 A, could be indicated with an arrow for easier detection. *

• Thanks for this suggestion, we will amend the figure.

Specify the type and location of NB imaged during live cell experiments.

• The NBs were imaged in the brain lobes, and we did not distinguish between type I and II NBs. We will add a sentence in the method section to clarify.

*Reviewer #3 (Significance (Required)): Expertise: Drosophila stem cells *

• Many thanks for the constructive comments.

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Referee #3

Evidence, reproducibility and clarity

The transmembrane protein Syndecan regulates stem cell nuclear properties and cell maintenance.

In this work, the authors investigate the role of the transmembrane protein Syndecan (Sdc) in nuclear organisation and stem cell maintenance. Theys show that Sdc knockdown in intestinal stem cells (ISCs) results in a reduction of the ISC pool as well as of their progeny. They hypothesise that these ISCs might get eliminated via cell death, however, expression of the apoptotic inhibitor DIAP1 only rescued ISC loss by 50%. Hence, they suggest that apoptosis can not account for the total decrease in ISCs observed upon Sdc loss. ISCs depleted from Sdc exhibited abnormal cytoplasmic and nuclear morphologies. As Sdc has previously been implicated in the abscission machinery in mammalian cultured cells, they tested if Sdc could be playing a similar role in the abscission of ISCs. However, ISCs were capable of undergoing cytokinesis. Next, they tested if Sdc depletion could be altering the linkage between the plasma membrane and the nucleus mediated by the Linker of Nucleoskeleton and Cytoskeleton (LINC) complex. However, individual knockdowns of the different components of the complex did not disrupt the nuclear morphology to the same extent as Sdc knockdown, suggesting that Sdc function may be independent of the LINC complex. Finally, they observed that Sdc-depleted ISCs exhibited DNA damage, suggesting that Sdc may play a role in DNA protection. The authors next tested if Sdc played similar roles in other stem cell types such as the female germline stem cells (fGSCs) and larval neural stem cells (NSCs). While Sdc depletion appeared dispensable for fGSC maintenance, it prolonged NSC divisions and altered the nuclear morphology of NSCs. Upon further investigations, they observed that the NSC's nuclear envelope was disrupted upon division, hence causing defects in the nuclear size ratio of NSC and their progeny. This study provides with interesting findings in the field and proves a new role for Sdc in the regulation of intestinal and neural stem cell maintenance. I would recommend this manuscript to be accepted if the authors address the following comments.

Major comments:

1. In Figure 2 A-B, Sdc RNAi should ideally have a UAS control transgene to match the number of UAS being expressed to that of Sdc RNAi, DIAP1. Otherwise, it is plausible that reduced RNAi expression of Sdc RNAi, DIAP1 animals is the cause of the partial rescue.

Staining against cell death markers such as Dcp-1 or TUNEL might also quantify the number of cells undergoing cell death in each of the genotypes. 2. " These phenotypes were observed both with and without DIAP1 expression (Figure 2C), indicating that these cell shapes are not caused by apoptosis."

Misleading, as DIAP overexpression in Sdc knockdown background only rescued apoptosis by 50%. Hence, it is possible that those cells undergoing morphological defects, protrusions and blebbing might still undergo death - also considering those morphological changes are typically observed in apoptotic cells... Therefore, to rule apoptosis out, these cells should be shown to be negative for cell death markers. 3. Show if Sdc is expressed in fGSCs - the lack of phenotype caused by Sdc knockdown might be due to lack of expression of Sdc. 4. "After confirming the presence of Sdc in neuroblasts (data not shown)."

Data should be shown. It would be of great interest for researchers if you showed a staining of different brain cell types (NBs, glia, neurons) and the Sdc expression patterns. 5. You show how Slc-depleted NBs have disrupted nuclear morphologies. However, does Slc KD in NB lineages affect their ability to self-renew and generate differentiated progeny? Is the number of NBs and of their progeny cells altered as it is for ISCs? 6. Does protection against DNA damage in an Slc knockdown background prevent the defects observed with the single knockdown and ISC elimination? 7. Any idea the similarities between ISC and NBs that can account for why Sdc knockdown has effects in those systems, while no effect was observed in the germ cells?

Minor comments:

1. Lamina invaginations, for example in Figure 3 A, could be indicated with an arrow for easier detection.
2. Specify the type and location of NB imaged during live cell experiments.

Significance

Expertise: Drosophila stem cells

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Referee #2

Evidence, reproducibility and clarity

Summary

Stem cell (SC) maintenance and proliferation are necessary for tissue morphogenesis and homeostasis. The basement membrane (BM) has been shown to play a key role in regulating stem cell behavior. In this work, the authors unravel a new connection between the receptor for BM components Syndecan (Sdc) and SC behavior, using Drosophila as model system. They show that Sdc is required for intestine stem cell (ISC) maintenance, as Sdc depletion results in their progressive loss. At a cellular level, they also find that Sdc depletion in ISCs affects cell survival, cell and nuclear shape, nuclear lamina and DNA damage. In addition, they show that the defects in shape are not related to cell death. They also find that Sdc depletion in neural stem cells also results in nuclear envelope remodeling during cell division. This is in contrast to what happens in female germline stem cells where Sdc does not seem to be required for their survival or maintenance.

In general, I believe that this work unravels a connection between Sdc and stem cell behavior. However, I think the study is still at a preliminary stage, as how Sdc regulates different facets of stem cell behavior remains unclear.

Major comments:

1. To clearly show that the cellular changes produced by loss of Sdc are not due to cell death, one should quantify the ISC area and shape of Sdc-depleted ISCs expressing DIAP1 and compare it to that of Sdc-depleted ISCs. As DIAP1 overexpression only partially rescues ISC loss due to Sdc depletion, one should show that the Sdc-depleted ISCs expressing DIAP1 that still show cellular changes are not dying, as overexpression of Diap1 might not be sufficient to completely rescue cell death in all Sdc-depleted ISCs. In fact, apoptosis in Sdc depleted guts and the ability of Diap1 overexpression to rescue cell death should be analyzed using markers of caspase activity, this will provide a better idea of the contribution of apoptosis to the phenotypes associated to Sdc depletion.
2. The authors show that ISC loss is associated with reduced cell density, suggesting that this is most likely due to failure in new cell production. What do they mean with cell production? Is this related to a problem in regulating cell division or to the fact that as some ISCs are lost by apoptosis there is progressively less ISCs or to a combination of both? I think that cell division should be monitored throughout time as well as cell death in ISCs.
3. The authors report that in contrast to what happens when Sdc is eliminated from ISCs, its elimination from EEs results in an increase in the number of these cells. An explanation for this result is missing.
4. The authors suggest that "Sdc function is unlikely to be fully accounted for by individual LINC complex proteins, although these proteins might act redundantly". Checking redundancy seems a straight forward experiment, which only requires the simultaneous expression of RNAis against several of these proteins. This would help to settle the implication of LINC complex proteins on Sdc function.
5. Although quantification of DNA damage, by immunolabelling with H2Av, reveals that knockdown of individual LINC complex components did not recapitulate the damage observed upon Sdc depletion (Fig.3G), the image shown in Fig.3F reflects much higher levels of H2Av in Msp300 RNAi cells compared to Sdc RNAi cells. Authors should clarify this. In addition, the consequences of the simultaneous elimination of more than one component of the LINC complex on DNA damage should be analyzed.
6. The authors claim that the fact that "DNA damage was found more frequently in Sdc-depleted ISCs with lamina invaginations compared to those without (Figure 3H), supports a model whereby the development of nuclear lamina invaginations precedes the acquisition of DNA damage". However, to me, these results show that there is a relation between these two phenotypes, but not that one precedes the other. In order to show which one is the possible cause and which the consequence, the authors should perform a time course of the appearance of each of these phenotypes.
7. When studying the role of Sdc in neural stem cells, the authors show that elimination of Sdc in neuroblasts also affect nuclear envelope and shape. Furthermore, in this case, they also show that Sdc elimination affects cell division. To look for a more conserved role of Sdc in stem cell behavior, I believe the authors should also analyze whether Sdc elimination in neural stem cells results in an increase in DNA damage, as it is the case in ISCs.
8. When analyzing a possible role of Sdc in fGSCs, quantification of germline stem cells and H2Av levels in control nosGal4 and nos>Sdc RNAi germaria should be done. In addition, it is not clear to me whether Sdc is in fact expressed in fGSCs.
9. The authors should show presence of Sdc in neuroblasts.

Significance

In general, although this work reveals that elimination of Sdc affects different aspects of intestinal and neural stem cell behavior, including cell survival, cell production, nuclear shape, nuclear lamina or DNA damage, their contribution to stem cell loss and interactions between them have not been analyzed in detail. The role of the basement membrane in stem cell behavior has been extensively studied. In particular, the role of syndecan in stem cell regulation has been primarily confined to cancer, muscle, neural and hematopoietic stem cells. Thus, the study here presented could extend the role of Sdc to intestinal stem cells and could potentially reveals a conserved role for Sdc in neural stem cell behavior. However, the problem with the data mentioned above, hinders the assessment of the significance of this work.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this paper the authors explore the function of Syndecan in Drosophila stem cells focussing primarily on the intestinal stem cells. They use RNAi knockdown to conclude that Syndecan is required for long term stem cell maintenance as its knockdown results in apoptosis. They suggest that this effect is independent of LINC complex proteins but is associated with changes to nuclear morphology and DNA damage. They go on to show that a similar impact on nuclear shape can be seen in larval neuroblasts but not in stem cells of the female germline.

Major Comments

The key conclusion that underpins the paper is that reduced Syndecan causes loss of stem cells. This is based entirely on evidence from cell-type specific RNAi using 3 independent RNAi lines. Overexpression has no phenotype and there is no analysis of loss of function mutants. SdcRNAi3 gives strong phenotypes that are statistically significant and is used throughout the paper. SdcRNAi2 gives comparatively moderate phenotypes which trend in the same direction but it is not clear if these are statistically significant (Fig S1). SdcRNAi line 1 appears to have very little effect (and if anything trends in the opposite direction in S1A). In addition, the knockdown efficiency of the three lines has not been assessed. Another possible concern given the dependence on RNAi3 is that the RNAi control line used is not an ideal match for the VDRC GD RNAi lines as it is in a different genetic background. In order to robustly draw conclusions: the phenotypes with RNAi lines 1 and 2 should be tested for significance; the extent of knockdown in each should be quantified either by qPCR in whole tissue knockdown, or by staining for protein levels if possible, to assess whether the variation in phenotypes is due to different knockdown levels. The use of a loss of function mutant in clones or tissue specific CRISPR-Cas9 KO or KD would also significantly increase confidence in the findings.

Similarly, the evidence for a lack of LINC protein role in the phenotype relies on single RNAi lines without validation of knockdowns. The authors should ideally validate these lines in this system or reference other studies that have validated the lines in this or other contexts.

Minor Comments

The figures are generally very clear but some of the IF image panels are very small and require significant on-screen enlargement to be legible. In particular in Figure 1B the cross section views make it difficult to assess expression in the different cell types (and don't show very many cells), could this be shown in wholemount or as separated channels in a supplementary figure? In addition, it would strengthen the argument to include counterstains for markers of the different cell types (particularly to distinguish ISC/EB from EE). This could include esg-lacZ to mark ISC/EBs or prospero for EEs. However, if a broader view of these panels makes it clearer that all epithelial cells are expressing Syndecan this may not be essential.

Syndecan is referred to throughout as a stem cell regulator. This implies that in certain contexts or in response to certain stimuli its expression may be altered to elicit a stem cell response but no examples of this are shown. Moreover, only knockdown and not overexpression gives phenotypes suggesting its role may be as a required protein than a regulator. Either examples of its expression being modulated in homeostasis or in response to a challenge could be included or the wording could be amended.

Expression of Syndecan in neuroblasts is described as data not shown, it would be better to include this for completeness.

In addition to the intestinal validation of the Syndecan RNAi lines, validation of knockdown in the germline would be valuable to support the conclusions of Fig S4 given differences of knockdown in the germline with some RNAi lines (although inclusion of Dicer in the driver line should have overcome this).

Significance

The study describes a potentially very interesting, novel link between Syndecan, nuclear shape and apoptosis in cycling cells that could have broad relevance. If fully validated this could have implications for other stem cell populations, including those in mammals and disease relevance in the context of cancer.

The paper is fundamentally descriptive in nature and so the level of significance hinges on the strength of evidence and how interesting the phenotype itself is. At this stage the audience will be primarily in the areas of fundamental research in biology of the nucleus and cytoskeleton. Defining the mechanistic link between Syndecan and nuclear morphology will be a critical next step and while not essential for this study would significantly increase the likely interest in the paper. In terms of significance in stem cell biology the distinction between a regulator and a requirement to prevent stem cell apoptosis is important and the lack of evidence for a context in which Syndecan plays a regulatory role somewhat detracts from the breadth of impact.

My field of expertise is in epithelial stem cell biology.

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Reply to the reviewers

RC-2023-02105R: Brunetta et al.,

IF1 is a cold-regulated switch of ATP synthase to support thermogenesis in brown fat

We are happy to submit our revised manuscript after considering the suggestions made by reviewers. The comments were overall positive, and the changes requested were mostly editorial. We have, nevertheless, added new experiments as quality controls. These experiments did not affect the main conclusions of our work. In addition, we also included two in vivo experimental models of gain and loss-of-function, to further address the physiological relevance of IF1 in BAT thermogenesis. We believe with these additional experiments, quality controls as well as in vivo models, our study has improved considerably. We hope our efforts will be appreciated by the reviewers and we make ourselves available to answer any further questions.

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

Summary: In the present manuscript, the authors present data in support of their primary discovery that "IF1 controls UCP1-dependent mitochondrial bioenergetics in brown adipocytes". The opening figure convincingly demonstrates that IF1 expression is cold-exposure dependent. They then go on to show that loss of IF1 has functional consequences that would be predicted based on IF1's know role as a regulator of ATP hydrolysis by CV. They go on to make a few additional claims, succinctly detailed in the Discussion section. Specific claims include the following: 1) IF1 is downregulated in cold-adapted BAT, allowing greater hydrolytic activity of ATP synthase by operating in the reverse mode; 2) when IF1 is upregulated in brown adipocytes in vitro mitochondria unable to sustain the MMP upon adrenergic stimulation, 3) IF1 ablation in brown adipocytes phenocopies the metabolic adaptation of BAT to cold, and 4) IF1 overexpression blunts mitochondrial respiration without any apparent compensator response in glycolytic activity. The claims described above are well supported by the evidence. The manuscript is very well written, figures are clear and succinct. Overall, the quality of the work is very high. Given that IF1 is implicated across many fields of study, the novel discovery of IF1 as a regulator of brown adipose mitochondrial bioenergetics will be of significance across several fields. That said, a few areas of concern were apparent. Concerns are detailed in the "Major" and "Minor" comments section below. Additional experiments do not appear to be required, assuming the authors adequately acknowledge the limitations of the study and either remove or qualify speculative claims.

Major Comments:

1. The authors convincingly demonstrate that IF1 expression is specifically down-regulated in BAT upon cold-exposure. These data strongly implicate a role for IF1 in BAT bioenergetics, a major claim of the authors and a novel finding herein. Additional major strengths of the paper, which provide excellent scientific rigor include the use of both loss of function and gain of function approaches for IF1. In addition, the mutant IF1 experiments are excellent, as they convincingly show that the effects of IF1 are dependent on its ability to bind CV. RESPONSE: We thank the reviewer for the positive feedback on our work.

Regarding Figure 1 - Did the content of ATP synthase change? In figure 1A-B, the authors show that ATPase activity of CV is higher in cold-adapted mice. While this result could be due to a loss of IF1, it could also be due to a higher expression of CV. To control for this, the authors should consider blotting for CV, which would allow for ATPase activity to be normalized to expression.

RESPONSE: Thank you for this suggestion. We have now determined complex V subunit A in our experimental protocol. We found that cold exposure does not impact complex V protein levels. Given the importance of this control, we have now included it in Figure 1 (Please, see the revised version) alongside the IF1/complex V ratio. In addition, we have now performed WBs in the BAT from mice exposed for 3 and 7 days to thermoneutrality (~28°C). We found that IF1 is not reduced following whitening of BAT by this approach whilst UCP1 and other mitochondrial proteins are reduced. This set of data is now included in Figure 1I,K,L.

Regarding MMP generated specifically by ATP hydrolysis at CV, the reversal potential for ANT occurs at a more negative MMP than that of CV (PMID: 21486564). Because reverse transport of ATP (cytosol to matrix) via ANT will also generate a MMP, it is speculative to state that the MMP in the assay is driven by ATP hydrolysis at CV. It is possible and maybe even likely that the majority of the MMP is driven by ANT flux, which in turn limits the amount of ATP hydrolyzed by CV. Admittedly, it is very challenging to different MMP from ANT vs that from CV, thus the authors simply need to acknowledge that the specific contribution of ATP hydrolysis to MMP remains to be fully determined. That said, the fact that ATP-dependent MMP tracks with IF1 expression does certainly implicate a role for ATP hydrolysis in the process. The authors should consider including a discussion of the ambiguity of the assay to avoid confusion. A role for ANT likely should be incorporated in the Fig. 1J cartoon.

RESPONSE: Thank you for bringing the ANT contribution to MMP to our attention. The effects of ATP in the real-time MMP measurements were totally abolished by the addition of oligomycin in BAT-derived isolated mitochondria, thus suggesting dependency of complex V in this process. However, the assessment of MMP in intact cells is much more challenging given cytosolic vs. mitochondrial contribution to ATP pool, and ATP synthase vs. ANT reversal capacity depending on MMP. Nevertheless, we have addressed these points in the discussion section as well as added to our schematic cartoon in Figure 1m.

Regarding the lack of effect of IF1 silencing on MMP, it is possible that IF1 total protein levels are simply lower in cultured brown fat cells relative to tissue? The authors could consider testing this by blotting for IF1 and CV in BAT and brown fat cells. The ratio of IF1/ATP5A1 in tissue versus cells may provide some amount of mechanistic evidence as to their findings.

RESPONSE: We have now blotted for complex V and IF1 in both differentiated primary brown adipocytes and BAT homogenates derived from mice kept at room temperature (~22°C). We found the levels of complex V in primary brown adipocytes are higher than BAT homogenates. Therefore, IF1/complex V ratio is different between these two systems. This has indeed the potential to influence our gain and loss-of-function experiments. We have added these results alongside their interpretation in the revised manuscript.

The calculation of ATP synthesis from respiration sensitive to oligomycin has many conceptual flaws. Unlike glycolysis, where ATP is produced via substrate level phosphorylation, during OXPHOS, the stoichiometry of ATP produced per 2e transfer is not known in intact brown adipose cells. This is a major limitation of this "calculated ATP synthesis" approach that is beginning to become common. Such claims are speculative and thus likely do more harm than good. In addition to ANT and CV, there are many proton-consuming reactions driven by the proton motive force (e.g., metabolite transport, Ca2+ cycling, NADPH synthesis). Although it remains unclear how much proton conductance is diverted to non-ATP synthesis dependent processes, it seems highly likely that these processes contribute to respiratory demand inside living cells. Moreover, just as occurs with UCP1 in response to adrenergic stimuli, proton conductance across the various proton-dependent processes likely changes depending on the cellular context, which is another reason why using a fixed stoichiometry to calculate how much ATP is produced from oxygen consumption is so highly flawed. Maximal P/O values that are often used for NAD/FAD linked flux are generated using experimental conditions that favor near complete flux through the ATP synthesis system (supraphysiological substrate and ADP levels). The true P/O value inside living cells is likely to be lower.

RESPONSE: We agree with the reviewer regarding the limitations on calculating ATP production in intact cells based on respiration and proton flux. However, this was only one experiment on which we based our conclusions, as these were also supported by i.e. ATP/ADP ratio measurements and oxygen consumption using different substrates. Therefore, we do not rely exclusively on the ATP production estimative, rather we use this experiment to support complementary methodologies. Nevertheless, we have now better detailed our experimental protocol as well as acknowledged the limitations of the method, so the reader is aware of our procedure and its limitations. We hope the reviewer understands our motivation to perform these experiments and the contribution to our study.

Why are the results in Figure 3K expressed as a % of basal? Could the authors please normalize the OCR data to protein and/or provide a justification for why different normalization strategies were used between 3K and 3M?

RESPONSE: We apologize for the lack of consistency. We have now updated Figure 3 to show all the data in absolute values divided by protein content. This change does not affect the overall interpretation of the findings.

The authors claim that IF1 overexpression lowers ATP production via OXPHOS. However, given the major limitations of this assay (ass discussed above), these claims should be viewed as speculation. This needs to be addressed by the authors as a major limitation. The fact that the ATP/ADP levels did not change do not support of reduction in ATP production, as claimed in the title of Figure 4.

RESPONSE: The reduction in ATP levels and mitochondrial respiration (independent of the substrate offered) suggests a reduction in ATP production rather than an increase in ATP consumption. Moreover, the maintenance of ATP/ADP ratio suggests the existence of a compensatory mechanism to avoid cellular energy crises, which we interpreted as reduced metabolic activity of the cells. Nevertheless, we have now reworded our statements to address the limitations of the methods and our interpretation of the data.

In the discussion, the authors state "However, considering that IF1 inhibits F1-ATP synthase in a 1:1 stoichiometric ratio, the relatively higher expression of IF1 in BAT at room temperature could represent an additional inhibitory factor for ATP synthesis in this tissue." This does not appear to be correct. Although IF1 has been suggested to partially lower maximal rates of ATP synthesis rates, most of this evidence comes from over-expression experiments. According to the current understanding of IF1-CV interaction, the protein is expelled from the complex during rotation in favor of ATP synthesis (PMID: 37002198). It is far more likely that ATP synthesis is low in BAT mitochondria due to the low CV expression. Relative to heart and when normalized to mitochondrial content, CV expression in BAT mitochondria is about 10% that of heart (PMID: 33077793).

RESPONSE: We agree with the reviewer and removed this sentence.

The last sentence of the manuscript states, "Given the importance of IF1 to control brown adipocyte energy metabolism, lowering IF1 levels therapeutically might enhance approaches to enhance NST for improving cardiometabolic health in humans." This sentence seems at odds with the evidence that IF1 levels go up, not down, in human BAT upon cold exposure.

RESPONSE: In light of our new experiments, we have now updated our conclusions.

Minor Comments:

The term "anaerobic glycolysis" is used throughout. All experiments were performed under normoxic conditions, thus the correct term is "aerobic glycolysis.

RESPONSE: Thank you for this comment and we have replaced this term as suggested.

Only male mice were used in the study, could the authors please provide a justification for this?

RESPONSE: Given we devoted most of our efforts to the manipulation of IF1 in vitro, we have used the mouse model as a proof-of-principle on the impact of IF1 in adrenergic-induced thermogenesis. We have now included IF1 KO male and female mice to address the role of IF1 in adrenergic-induced thermogenesis. However, due to the limitation of material, we could only perform AAV in vivo gain-of-function in male mice, therefore, our results cannot be immediately transferred to both sexes, unfortunately.

Reviewer #1 (Significance (Required)):

Overall, the quality of the work is very high. Given that IF1 is implicated across many fields of study, the novel discovery of IF1 as a regulator of brown adipose mitochondrial bioenergetics will be of significance across several fields.

My expertise is in mitochondrial thermodynamics; thus, I do not feel there are any parts of the paper that I do not have sufficient expertise to evaluate.

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

Summary

The manuscript by Brunetta and colleagues conveys the message that the ATPase inhibitory factor 1 (IF1) protein, a physiological inhibitor of mitochondrial ATP synthase, is expressed in BAT of C57BL/6J mice. Moreover, upon cold-adaption of mice they report that the content of IF1 in BAT is downregulated to sustain the mitochondrial membrane potential (MMP) as a result of reverse functioning of the enzyme. In experiments of loss and gain of function of IF1 in cultured brown adipocytes and WT cells they further stress that IF1 silencing promotes metabolic reprogramming to an enhanced glycolysis and lipid oxidation, whereas IF1 overexpression blunts ATP production rendering a quiescent cellular state of the adipocytes.

RESPONSE: We appreciate the time the reviewer invested in our work. Please, see our responses below in a point-by-point manner.

Reviewer #2 (Significance (Required)):

Claims and conclusions:

I have been surprised by the claim that IF1 protein is expressed in BAT under basal conditions and that its expression is downregulated in the cold-adapted tissue. In a previously published work by Forner et al., (2009) Cell Metab 10, 324-335 (reference 43), using a quantitative proteomic approach, it is reported that the mitochondrial proteome of mouse BAT under basal conditions contains a low content of IF1 (at level comparable to the background of the analysis). Remarkably, in the same study they show that there is roughly a 2-fold increase in the content of IF1 protein in mitochondria of BAT at 4d and 24d of cold-adaptation of mice. In other words, just the opposite of what is being reported in the Brunetta study.

RESPONSE: We are aware of the inconsistencies between our findings and Forner et al. (2009). We would like to point out that we have determined IF1 levels in BAT in two separate cohorts with the same findings, and in a third cohort, we observed IF1 mRNA levels to be downregulated in a much shorter timeframe. Our functional analysis is line with this pattern of regulation. A closer look at the supplementary table provided by Forner et al. (2009), shows that the increase in IF1 content following cold exposure is not supported and since we do not have further insight into the methods and analysis employed by the Forner et al. group, we believe a direct comparison should be avoided at the moment. Regarding the baseline levels of IF1 in BAT, the relatively high abundance of IF1 in BAT was also found by another independent group (https://doi.org/10.1101/2020.09.24.311076).

Importantly, the last paragraph of the discussion needs to be amended when mentioning the work of Forner et al. (ref.43). The mentioned reference studied changes in the mouse mitochondrial proteome not in human mitochondria, as it is stated in the alluded paragraph.

RESPONSE: We apologize for this overlook; we have now reworded our statement.

More puzzling are the western blots in Figures 1E, 1H, Supp. Fig. 1C, D were IF1 (ATP5IF1) is identified by a 17kDa band. However, in other Figures (Fig. 2, Fig. 3, Fig. 4, Supp Fig. 2) IF1 is identified by its well-known 12kDa band. What is the reason for this change in labeling of the IF1 band? The reactivity of the anti-IF1 antibody used? It has been previously documented that liver of C57BL/6J and FVB mouse strains do not express IF1 to a significant level when compared to heart IF1 levels (Esparza-Molto (2019) FASEB J. 33, 1836-1851). However, in Fig. 1E they show opposite findings, much higher levels of IF1 in liver than in heart as reveal by the 17kDa band. Moreover, in Fig. 1H they show the vanishing of the 17 kDa band under cold adaptation, which is not the migration of IF1 in gels as shown in their own figures (see Fig. 2, Fig. 3, Fig. 4, Supp Fig. 2). I am certainly reluctant to accept that the 17kDa band shown in Figures 1E, 1H, Supp. Fig. 1C, D is indeed IF1. Most likely it represents a non-specific protein recognized by the antibody in the tissue extracts analyzed. Cellular overexpression experiments of IF1 in WT1 cells (Fig. 2E) and primary brown adipocytes (Fig. 4B) also support this argument. Overall, I do not support publication of this study for the reasons stated above.

RESPONSE: We understand the concerns raised by the reviewer and apologize for the lack of details in our experimental procedures. While we used the same antibody in the study (Cell Sig. cat. Num. 8528, 1:500), we used two different types of gels. The difference in the molecular weight appearance of IF1 is likely through the migration of the protein in the agarose gel. By using custom-made gels, we observe the protein ~17kDa (Fig. 1 and 5), whereas by using commercial gels (Fig. 2, 3, and 4), we observe the protein closer to the predicted molecular weight (i.e. ~12kDa). Of note, gain and loss-of-function experiments, both in vivo as well as in vitro confirm this statement and the specificity of the antibody (Fig. 2, 3, 4, 5, Fig. EV2). In addition, when we ran a custom-made gel with primary BAT cells, we observed again the ~17kDa band (see Figure for the reviewer below). These experiments alongside the absence of other bands in the gels (see uncropped membranes in Supplementary Figure 1) make us conclude that the band we observe is indeed IF1. Nevertheless, we have now updated our methods section, so the reader is aware of our approaches. We hope the reviewer is satisfied with our additional experiments and editions throughout the manuscript.

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

Summary:

In this manuscript, Brunneta et al describe the role of IF1 in brown adipose tissue activation using in vivo and in vitro experimental models. They observed that cold adaptation promotes a reduction in IF1 expression and an increase in the reverse activity of mitochondrial ATPase or Complex V. Based on these results, the authors explore the contribution of IF1 in this metabolic pathway by modeling the thermogenic process in differentiated primary brown adipocytes. They silenced and overexpressed IF1 in culture and studied their adrenergic stimulation under norepinephrine.

Major comments:

The experiments are well explained and the manuscript flows very well. There are several comments that should be addressed.

RESPONSE: We thank the reviewer for the kind words regarding our work.

1. The authors measure ATP hydrolysis in isolated mitochondria from BAT in Figure 1. They observed that IF1 is decreased upon cold exposure and that ATP hydrolysis is increased. They assess protein levels of different OXPHOS proteins, including IF1 but not other proteins of Complex V (ATP5A) as they do in Figures 3 and 4. It is important to see that cold exposure only affects IF1 levels but not other proteins from Complex V. Does IF1/Complex V ratio change? RESPONSE: We thank the reviewer for this suggestion which was also raised by Reviewer #1. We have now measured complex V subunit A in our experimental protocol. We found that cold exposure does not impact complex V protein levels. Given the importance of this information, we have now included it in Figure 1 (Please, see the revised version) alongside the IF1/complex V ratio. In addition, we have now performed WBs in the BAT exposed for 3 and 7 days to thermoneutrality (~28°C) where we found that IF1 is not reduced following whitening of BAT by this approach whilst UCP1 and other mitochondrial proteins are reduced.

This set of data is now included in Figure 1I,K,L.

In Figure 2J, the drop in MMP is lower upon adrenergic stimulation than in Figure 2E. The same observation applies to other results when the reduction in MMP after NE addition is minimal. Why do the authors remove TMRM for the measurements of membrane potential? TMRM imaging is normally done in the presence of the dye in non-quenching mode. Treatments should be done prior to the addition of the dye and then TMRM should be added and left during the imaging analysis and measure in non-quenching mode. This might explain some of the above-mentioned points regarding the MMP data. Alternatively, if the dye is removed before the measurements, they should let the cells to adapt and so the dye equilibrates between mitochondria and cytosol. A more elegant method to measure membrane potential could be live-cell imaging. In addition, authors propose that mitochondrial membrane potential upon NE stimulation is maintained by reversal of ATP synthase. If this is the case, one would expect that addition of oligomycin in NE treated adipocytes would cause depolarization. However, in FigS2A this is not the case. Authors should comment on this in addition to considering more elegant approach to measure MMP.

RESPONSE: We apologize for the lack of details in the methods. All treatments (i.e., transfection and norepinephrine stimulation) were performed before the addition of TMRM. Indeed, this approach does not have the resolution compared to safranine in isolated mitochondria (Fig. 1D), which limits our interpretation regarding the dynamic role of IF1 on MMP in brown adipocytes. We have taken care to state the limitations of our method throughout the entire paper to avoid overinterpretation of our data. Regarding the removal of the dye before the measurements, our internal controls indicate that this procedure does not change the ability of our method to detect fluctuations in MMP (i.e., oligomycin and FCCP as internal controls). Nevertheless, as suggested by the reviewer, to test the time effect of the probe equilibrium (i.e., mitochondria versus cytosol) in our method, we loaded cells with TMRM 20 nM for 30 min and measured the fluorescence right after the removal of the probe/washing steps for another 10 min. We were not able to detect differences in the fluorescence in a time-dependent manner (see below). Therefore, we conclude the removal of TMRM does not influence the fluorescence of the probe in differentiated brown adipocytes.

+NE

-NE

In addition, we performed a similar experiment using TMRM in the quenching mode (200 nM), however, after the removal of TMRM, we added FCCP (1 mM) to the cells for 10 min under constant agitations at 37°C. This approach aimed to expel all TMRM that accumulated within the mitochondria in an MMP-dependent manner. Therefore, excluding the dynamic Brownian movement that we could have caused by the removal of the dye before the measurement mentioned by the reviewer. By doing this, we found the same effect of IF1 overexpression in the reduction of MMP in the presence of norepinephrine.

Protocol:

• Transfection (24h) on day 4 of differentiation + 24h just normal media

• 30 min norepinephrine 10 µM

• 200 nM TMRM on top of NE

• Washing step

• Add FCCP 1 µM for 10 min, and read (The aim here was to release all TMRM accumulated inside of mitochondria in a MMP-dependent manner)

In summary, the data suggests the removal of the dye from the cells does not influence the fluorescence of TMRM, therefore, enabling us to make conclusions regarding the biological effects of IF1 manipulation in the MMP of brown adipocytes. Regarding the reverse mode of ATP synthase and the absence of effects with oligomycin, given oligomycin inhibits both rotation of ATP synthase and even uncoupled brown adipocytes respond to oligomycin (i.e. reduction in O2 consumption), the prediction of lowering MMP in the presence of oligomycin due to inhibition of the reserve mode of ATP synthase is more complicated than anticipated. Nevertheless, we have now addressed this topic in the discussion section. Lastly, we generally observe a reduction in MMP around 10-25% in differentiated adipocytes upon NE treatment (30 minutes, 10mM). However, due to the differentiation state of the cells, MMP response from norepinephrine fluctuated from experiment to experiment. Therefore, we did not compare experiments performed on different days or batches, but only within the same differentiation batch to reduce variability.

In Figure 2, in the model of siIF1, there is baseline more phosphorylation of AMPK than in the scramble control (pAMPK). However, this is not the case of p-p38MAPK. Do the authors have any explanation for those differences in baseline activation of the stress kinases when IF1 is silenced? In the same experimental group, addition of NE seems to have more effect in the scrambled than in siIF1, but the plotted data does not reflect these differences. In contrast, increase in pAMPK upon NE is higher in IF1 overexpressing cells compared to EV (Figure 2H), but again this is not reflected in western blot quantification (Figure 2I).

RESPONSE: Although some differences in pAMPK in the treatments were observed as gathered by the representative blots, these changes were not confirmed later in different biological replicates, therefore, the overall effect of IF1 manipulation in pAMPK does not change. Given we used this approach as quality control for our experiments to guarantee norepinephrine treatment works, we removed the pAMPK data from the study and kept p38 as a marker of adrenergic signaling activation (please see revised Fig. 2 in the main file).

Does NE promote decrease of IF1 expression in control (siScramble and EV) adipocytes? The authors should test it and see whether it goes in the same direction as the observations derived from the experiments in cold exposed mice. This is very important point, as it could explain the lack of an additional effect of IF1 silencing on NE-induced depolarization (Figure 2E).

RESPONSE: We thank the reviewer for this suggestion. In line, with the in vivo data, acute NE treatment in differentiated brown adipocytes does not change IF1 mRNA and protein levels. We have now added this information and the corresponding interpretation to the updated manuscript.

Does NE promote decrease of IF1 expression in the scramble and EV adipocytes? The authors should test it and see whether it goes in the same direction as the observations derived from the experiments in cold exposed mice.

RESPONSE: As this question is the same as #4, we believe the reviewer may have erroneously pasted this here.

For MMP data in Fig2, they should include significance between non treated and NE-treated groups. They say: "While UCP1 ablation did not cause any effect on MMP upon adrenergic stimulation...", but NE caused (probably significant) depolarization in siUCP1, which seems even stronger than depolarization in EV. This is opposite to what you would expect. They also didn't confirm UCP1 silencing with western blot.

RESPONSE: We thank the reviewer for this suggestion. We have now included the expected statistical main effect of NE upon MMP. Although the effects of IF1 overexpression were blunted when Ucp1 was silenced, we indeed still observed the same degree of reduction in MMP in brown adipocytes. This finding has two possible explanations, one is the effectiveness of the silencing protocol, therefore, residual Ucp1 expression may still play a role in this experiment; second, other ATP-consuming processes are able to lower MMP in a UCP1-independent manner. We have added this information to the updated manuscript to make the reader aware of our findings as well as the limitations of the method. Unfortunately, we were not able to detect UCP1 protein levels due to technical issues. Given the effects of IF1 overexpression were blunted when Ucp1 was silenced, we believe this functional outcome is sufficient, alongside mRNA levels, to demonstrate the effectiveness of our silencing protocol.

It has been established that decreased expression of IF1 promotes increase in the reverse activity of Complex V, ATP hydrolytic activity. Increase in ATP hydrolysis also affects ECAR. The authors should consider this when calculating the contribution of ATP glycolysis versus ATP OXPHOS since the ATP hydrolysis is also playing a role in the ECAR increase. The data should be reinterpreted. ATP hydrolysis should be measured in the situation where IF1 is silenced and overexpressed. These measurements can be done in cells using the seahorse.

RESPONSE: The only differences we observed in MMP are in the presence of norepinephrine (i.e. UCP-1-dependent proton conductance), which is not present during the estimation of ATP production by Seahorse analysis. Nevertheless, we have now improved the description of our experimental protocol and limitations to estimate ATP production to make it as clear as possible to the reader. Lastly, given the addition of in vivo gain-of-function experiments, we have now determined the ATP hydrolytic activity in this model, which offers a better understanding of the in vivo modulation of IF1 levels affecting ATP synthase activity (reverse mode). We hope the reviewer understands our motivation to focus on the in vivo model of gain-of-function regarding ATP synthase activity.

The authors use GAPDH as loading control in western blots. They should use another protein since GAPDH is part of the intermediary metabolism and plays a role in glycolysis.

RESPONSE: We understand the concern of the reviewer regarding the use of GAPDH as a loading control for the studies of metabolism. However, as can be observed by the western blot images, GAPDH levels do not change in our experimental models, therefore, we feel confident that our loading is homogeneous throughout our gels.

The authors show that reduction of IF1 involves more lipid utilization. They should include more experiments showing the connection of the metabolic adaptation in the absence of IF1 and some lipid imaging.

RESPONSE: We appreciate this suggestion. We have now performed Oil Red O staining in differentiated adipocytes following ablation of IF1. However, we did not observe any effect on lipid accumulation in primary brown adipocytes following IF1 knockdown. Therefore, the effects of IF1 ablation on lipid mobilization are not due to lipid content or reflected in lipid accumulation. We have now added this new information to the manuscript (please, see the revised form Fig. EV3).

In the text, "Despite this adjustment of experimental conditions, we did not detect any effect of IF1 ablation on mitochondrial oxygen consumption (Supplementary Fig. 3A,B)", this is true for baseline, NE-driven and ATP-linked respiration, but what about maximal respiration? There is a huge increase in IF1 knockdown... They should explain these results.

RESPONSE: We perform this experiment to address the question of whether the lipid mobilization induced by norepinephrine would uncouple mitochondria in a UCP1-independent manner. Given the absence of effect between scrambled and IF1 ablated cells in mitochondrial respiration in the presence of norepinephrine and following the addition of oligomycin, we concluded no effect of lipolysis-induced UCP1-independent uncoupling. However, as observed by the reviewer and consistent with other data within the study, the interaction between lipid metabolism and IF1 knockdown seems to affect maximal electron transport chain activity, which although interesting, was not the focus of the present study. Nevertheless, we have now acknowledged these findings and a possible explanation for them in the revised manuscript.

In Figure 3K they present OCR as % of baseline, but in a similar experiment in Figire 4G it is OCR/protein, they should make the Y axis consistent across experiments.

RESPONSE: We apologize for this overlook. We have now edited all the axes and labels for consistency.

The graphical abstract is confusing. In BAT there are two populations of mitochondria, the cytosolic and the mitochondria attached to the lipid droplet, peridroplet mitochondria (PDM). Upon adrenergic stimulation, PDM leave the lipid droplet and lipolysis takes place. The authors propose that upon adrenergic stimulation, IF1 is reduced and there is lipid mobilization. The part of the scheme where it says "fully recruited" should be removed or rewritten, since adrenergic stimulation is not compatible with mitochondria recruitment around the lipid droplet.

RESPONSE: Thank you for this input. Given the addition of new experiments and interpretation, we have now redrawn the graphical abstract and addressed this topic in the discussion section.

The title should be rewritten to better reflect the research presented in the manuscript.

RESPONSE: Thank you for this input. Given the addition of new experiments, we have now rewritten the title accordingly.

Minor comments:

Some of the Y axis should be corrected. For example, in Figure 2J, L and M should say % of EV untreated, Similarly, in Figure 2E, it should say % of scramble untreated. In Figure 3N, the Y axis is misspelled. All the Y axis referring to percentages should have the same scale for comparison purposes.

RESPONSE: Thank you for the proofreading. We have now edited the scales and labels to keep consistency.

The authors should describe better the results corresponding to Figure 2. There is a lot of information and they should improve the description pertaining the connection between the different pieces of data relating the different signaling pathways that are shown. For westerns in this Figure, they should provide some rationale (one to two sentences in the results section) as to why they are checking the expression of pAMPK and p38-MAPK.

RESPONSE: We have now edited the description of our results to make them as clear as possible.

Here are some comments referring to the methods section:

For Complex V hydrolytic activity, the reaction buffer contains 10mM Na-azide. I guess this is to inhibit respiration, but wouldn't azide also inhibit complex V at this concentration?

RESPONSE: We thank the reviewer for this question. To test that, we performed complex V activity in buffers containing or not 10 mM sodium azide. As demonstrated below, the presence of sodium azide in the buffer does not influence complex V activity in two different tissues with low and high complex V activity (BAT and heart, respectively).

Table 1. ATP synthase hydrolytic activity in the presence or absence of Na-azide.

BAT

Heart

+Na-azide

100 ± 43.01

100 ± 39.36

-Na-azide

82.6 ± 4.33

111.3 ± 43.32

+Na-azide + oligomycin

15.3 ± 4.32*

13.8 ± 14.01*

-Na-azide + oligomycin

14.2 ± 3.53*

11.9 ± 2.88*

Data presented as % of control (i.e. presence of Na-azide and absence of oligomycin) for both tissues independently. N = 2-3/condition. Statistical test: two-way ANOVA. * main effect of oligomycin (p In the mitochondrial isolation protocol, they say "mitochondria were centrifuged at 800g for 10min..." Will this speed pellet the mitochondria? I think this is a mistake in writing.

RESPONSE: We apologize for the lack of clarity. What was centrifuged at 800 g was the whole-tissue homogenate to discard cellular debris, before pelleting mitochondria at 5000 g. We have now corrected this mistake in the methods section.

For the safranin-O experiment, they don't mention mitochondrial substrate used, probably it's in the reference that they provide, but I think it should be included in the text.

RESPONSE: We did not use any substrate because our goal was to test the contribution of ATP synthase to mitochondrial membrane potential. For that, we inhibited proton movement within the ETC with antimycin A and through UCP1 with GDP (see Methods). We have now edited our Method’s description to make sure the reader is aware of our approach.

Reviewer #3 (Significance (Required)):

The manuscript is well written, and it flows well when reading. However, there are some additional experiments that need to be performed to reach the conclusions the authors claim.

RESPONSE: We thank the reviewer for the positive commentaries regarding our work and hope to have answered the open questions with the edits and new experiments.

The role of ATP hydrolysis in BAT thermogenesis is novel and interesting as it can sed some light onto potential approaches to promotes BAT activation.

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

This is an interesting investigation into the activity of IF1 in brown adipocytes. The findings are innovative and the conclusion is well-supported by the data. The conclusion is in line with previous reports on IF1 activities in other cell types, particularly in terms of its regulation of FoF1-ATPase. The authors have executed an exceptional job in designing the study, preparing the figures, and writing the manuscript. Overall, this study significantly contributes to the understanding of IF1 activity in brown adipocytes and its role in thermogenesis.

RESPONSE: We thank the reviewer for the kind words. Please, find below our answers in a point-by-point manner.

Reviewer #4 (Significance (Required)):

The study demonstrates involvement of IF1 in regulating thermogenesis in brown adipocytes, which is a unique aspect not covered in existing literature. Advantage of the study is well-designed cellular studies. The major weakness is lack of proof of conclusion in vivo. There are a few minor concerns that should be addressed to further enhance quality of the manuscript.

RESPONSE: We have now included two in vivo models, whole-body IF1 KO mice and BAT-injected IF1 overexpression to test the role of IF1 in BAT biology. The whole dataset is included in the main manuscript, where we conclude the BAT IF1 overexpression partially suppresses b3-adrenergic induction of thermogenesis alongside a reduction (overall and UCP1 dependent) in mitochondrial oxygen consumption. Also, similar to our in vitro experiments, IF1 KO mice did not present any difference in adrenergic-stimulated oxygen consumption.

1. Current discussion does not mention the regulation of IF1 protein by the cAMP/PKA pathway. This point should be included to provide a comprehensive understanding of the regulatory mechanisms of IF1 protein. RESPONSE: Thank you for this suggestion. We have now added this topic to the discussion.

It has been reported that IF1 also influences the structure of mitochondrial crista. Considering the observed changes with IF1 knockdown, it would be valuable to discuss this activity in relation to the findings of the study.

RESPONSE: We discussed the implications of IF1 modulation in mitochondrial morphology in the revised manuscript.

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

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Referee #4

Evidence, reproducibility and clarity

This is an interesting investigation into the activity of IF1 in brown adipocytes. The findings are innovative and the conclusion is well-supported by the data. The conclusion is in line with previous reports on IF1 activities in other cell types, particularly in terms of its regulation of FoF1-ATPase. The authors have executed an exceptional job in designing the study, preparing the figures, and writing the manuscript. Overall, this study significantly contributes to the understanding of IF1 activity in brown adipocytes and its role in thermogenesis.

Significance

The study demonstrates involvement of IF1 in regulating thermogenesis in brown adipocytes, which is a unique aspect not covered in existing literature.Advantage of the study is well-designed cellular studies. The major weakness is lack of proof of conclusion in vivo. There are a few minor concerns that should be addressed to further enhance quality of the manuscript.

1. Current discussion does not mention the regulation of IF1 protein by the cAMP/PKA pathway. This point should be included to provide a comprehensive understanding of the regulatory mechanisms of IF1 protein.
2. It has been reported that IF1 also influences the structure of mitochondrial crista. Considering the observed changes with IF1 knockdown, it would be valuable to discuss this activity in relation to the findings of the study.

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

Learn more at Review Commons

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript, Brunneta et al describe the role of IF1 in brown adipose tissue activation using in vivo and in vitro experimental models. They observed that cold adaptation promotes a reduction in IF1 expression and an increase in the reverse activity of mitochondrial ATPase or Complex V. Based on these results, the authors explore the contribution of IF1 in this metabolic pathway by modeling the thermogenic process in differentiated primary brown adipocytes. They silenced and overexpressed IF1 in culture and studied their adrenergic stimulation under norepinephrine.

Major comments:

The experiments are well explained and the manuscript flows very well. There are several comments that should be addressed.

1. The authors measure ATP hydrolysis in isolated mitochondria from BAT in Figure 1. They observed that IF1 is decreased upon cold exposure and that ATP hydrolysis is increased. They assess protein levels of different OXPHOS proteins, including IF1 but not other proteins of Complex V (ATP5A) as they do in Figures 3 and 4. It is important to see that cold exposure only affects IF1 levels but not other proteins from Complex V. Does IF1/Complex V ratio change?
2. In Figure 2J, the drop in MMP is lower upon adrenergic stimulation than in Figure 2E. The same observation applies to other results when the reduction in MMP after NE addition is minimal. Why do the authors remove TMRM for the measurements of membrane potential? TMRM imaging is normally done in the presence of the dye in non-quenching mode. Treatments should be done prior to the addition of the dye and then TMRM should be added and left during the imaging analysis and measure in non-quenching mode. This might explain some of the above-mentioned points regarding the MMP data. Alternatively, if the dye is removed before the measurements, they should let the cells to adapt and so the dye equilibrates between mitochondria and cytosol. A more elegant method to measure membrane potential could be live-cell imaging. In addition, authors propose that mitochondrial membrane potential upon NE stimulation is maintained by reversal of ATP synthase. If this is the case, one would expect that addition of oligomycin in NE treated adipocytes would cause depolarization. However, in FigS2A this is not the case. Authors should comment on this in addition to considering more elegant approach to measure MMP
3. In Figure 2, in the model of siIF1, there is baseline more phosphorylation of AMPK than in the scramble control (pAMPK). However, this is not the case of p-p38MAPK. Do the authors have any explanation for those differences in baseline activation of the stress kinases when IF1 is silenced? In the same experimental group, addition of NE seems to have more effect in the scrambled than in siIF1, but the plotted data does not reflect these differences. In contrast, increase in pAMPK upon NE is higher in IF1 overexpressing cells compared to EV (Figure 2H), but again this is not reflected in western blot quantification (Figure 2I).
4. Does NE promote decrease of IF1 expression in control (siScramble and EV) adipocytes? The authors should test it and see whether it goes in the same direction as the observations derived from the experiments in cold exposed mice. This is very important point, as it could explain the lack of an additional effect of IF1 silencing on NE-induced depolarization (Figure 2E).
5. Does NE promote decrease of IF1 expression in the scramble and EV adipocytes? The authors should test it and see whether it goes in the same direction as the observations derived from the experiments in cold exposed mice.
6. For MMP data in Fig2, they should include significance between non treated and NE-treated groups. They say: "While UCP1 ablation did not cause any effect on MMP upon adrenergic stimulation...", but NE caused (probably significant) depolarization in siUCP1, which seems even stronger than depolarization in EV. This is opposite to what you would expect. They also didn't confirm UCP1 silencing with western blot.
7. It has been establish that decreased expression of IF1 promotes increase in the reverse activity of Complex V, ATP hydrolytic activity. Increase in ATP hydrolysis also affects ECAR. The authors should consider this when calculating the contribution of ATP glycolysis versus ATP OXPHOS since the ATP hydrolysis is also playing a role in the ECAR increase. The data should be reinterpreted. ATP hydrolysis should be measured in the situation where IF1 is silenced and overexpressed. These measurements can be done in cells using the seahorse.
8. The authors use GAPDH as loading control in western blots. They should use another protein since GAPDH is part of the intermediary metabolism and plays a role in glycolysis.
9. The authors show that reduction of IF1 involves more lipid utilization. They should include more experiments showing the connection of the metabolic adaptation in the absence of IF1 and some lipid imaging.
10. In the text, "Despite this adjustment of experimental conditions, we did not detect any effect of IF1 ablation on mitochondrial oxygen consumption (Supplementary Fig. 3A,B)", this is true for baseline, NE-driven and ATP-linked respiration, but what about maximal respiration? There is a huge increase in IF1 knockdown... They should explain these results.
11. In Figure 3K they present OCR as % of baseline, but in a similar experiment in Figire 4G it is OCR/protein, they should make the Y axis consistent across experiments.
12. The graphical abstract is confusing. In BAT there are two populations of mitochondria, the cytosolic and the mitochondria attached to the lipid droplet, peridroplet mitochondria (PDM). Upon adrenergic stimulation, PDM leave the lipid droplet and lipolysis takes place. The authors propose that upon adrenergic stimulation, IF1 is reduced and there is lipid mobilization. The part of the scheme where it says "fully recruited" should be removed or rewritten, since adrenergic stimulation is not compatible with mitochondria recruitment around the lipid droplet.
13. The title should be rewritten to better reflect the research presented in the manuscript.

Minor comments:

1. Some of the Y axis should be corrected. For example, in Figure 2J, L and M should say % of EV untreated, Similarly, in Figure 2E, it should say % of scramble untreated. In Figure 3N, the Y axis is misspelled. All the Y axis referring to percentages should have the same scale for comparison purposes.
2. The authors should describe better the results corresponding to Figure 2. There is a lot of information and they should improve the description pertaining the connection between the different pieces of data relating the different signaling pathways that are shown. For westerns in this Figure, they should provide some rationale (one to two sentences in the results section) as to why they are checking the expression of pAMPK and p38-MAPK.

Here are some comments referring to the methods section:

1. For Complex V hydrolytic activity, the reaction buffer contains 10mM Na-azide. I guess this is to inhibit respiration, but wouldn't azide also inhibit complex V at this concentration?
2. In the mitochondrial isolation protocol, they say "mitochondria were centrifuged at 800g for 10min..." Will this speed pellet the mitochondria? I think this is a mistake in writing.
3. For the safranin-O experiment, they don't mention mitochondrial substrate used, probably it's in the reference that they provide, but I think it should be included in the text.

Significance

The manuscript is well written, and it flows well when reading. However, there are some additional experiments that need to be performed to reach the conclusions the authors claim.

The role of ATP hydrolysis in BAT thermogenesis is novel and interesting as it can sed some light onto potential approaches to promotes BAT activation.

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Referee #2

Evidence, reproducibility and clarity

Summary

The manuscript by Brunetta and colleagues conveys the message that the ATPase inhibitory factor 1 (IF1) protein, a physiological inhibitor of mitochondrial ATP synthase, is expressed in BAT of C57BL/6J mice. Moreover, upon cold-adaption of mice they report that the content of IF1 in BAT is downregulated to sustain the mitochondrial membrane potential (MMP) as a result of reverse functioning of the enzyme. In experiments of loss and gain of function of IF1 in cultured brown adipocytes and WT cells they further stress that IF1 silencing promotes metabolic reprogramming to an enhanced glycolysis and lipid oxidation, whereas IF1 overexpression blunts ATP production rendering a quiescent cellular state of the adipocytes.

Significance

Claims and conclusions:

I have been surprised by the claim that IF1 protein is expressed in BAT under basal conditions and that its expression is downregulated in the cold-adapted tissue. In a previously published work by Forner et al., (2009) Cell Metab 10, 324-335 (reference 43), using a quantitative proteomic approach, it is reported that the mitochondrial proteome of mouse BAT under basal conditions contains a low content of IF1 (at level comparable to the background of the analysis). Remarkably, in the same study they show that there is roughly a 2-fold increase in the content of IF1 protein in mitochondria of BAT at 4d and 24d of cold-adaptation of mice. In other words, just the opposite of what is being reported in the Brunetta study. Importantly, the last paragraph of the discussion needs to be amended when mentioning the work of Forner et al. (ref.43). The mentioned reference studied changes in the mouse mitochondrial proteome not in human mitochondria, as it is stated in the alluded paragraph.

More puzzling are the western blots in Figures 1E, 1H, Supp. Fig. 1C, D were IF1 (ATP5IF1) is identified by a 17kDa band. However, in other Figures (Fig. 2, Fig. 3, Fig. 4, Supp Fig. 2) IF1 is identified by its well-known 12kDa band. What is the reason for this change in labeling of the IF1 band? The reactivity of the anti-IF1 antibody used? It has been previously documented that liver of C57BL/6J and FVB mouse strains do not express IF1 to a significant level when compared to heart IF1 levels (Esparza-Molto (2019) FASEB J. 33, 1836-1851). However, in Fig. 1E they show opposite findings, much higher levels of IF1 in liver than in heart as reveal by the 17kDa band. Moreover, in Fig. 1H they show the vanishing of the 17 kDa band under cold adaptation, which is not the migration of IF1 in gels as shown in their own figures (see Fig. 2, Fig. 3, Fig. 4, Supp Fig. 2). I am certainly reluctant to accept that the 17kDa band shown in Figures 1E, 1H, Supp. Fig. 1C, D is indeed IF1. Most likely it represents a non-specific protein recognized by the antibody in the tissue extracts analyzed. Cellular overexpression experiments of IF1 in WT1 cells (Fig. 2E) and primary brown adipocytes (Fig. 4B) also support this argument.

Overall, I do not support publication of this study for the reasons stated above.

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Referee #1

Evidence, reproducibility and clarity

Summary: In the present manuscript, the authors present data in support of their primary discovery that "IF1 controls UCP1-dependent mitochondrial bioenergetics in brown adipocytes". The opening figure convincingly demonstrates that IF1 expression is cold-exposure dependent. They then go on to show that loss of IF1 has functional consequences that would be predicted based on IF1's know role as a regulator of ATP hydrolysis by CV. They go on to make a few additional claims, succinctly detailed in the Discussion section. Specific claims include the following: 1) IF1 is downregulated in cold-adapted BAT, allowing greater hydrolytic activity of ATP synthase by operating in the reverse mode; 2) when IF1 is upregulated in brown adipocytes in vitro mitochondria unable to sustain the MMP upon adrenergic stimulation, 3) IF1 ablation in brown adipocytes phenocopies the metabolic adaptation of BAT to cold, and 4) IF1 overexpression blunts mitochondrial respiration without any apparent compensator response in glycolytic activity. The claims described above are well supported by the evidence. The manuscript is very well written, figures are clear and succinct. Overall, the quality of the work is very high. Given that IF1 is implicated across many fields of study, the novel discovery of IF1 as a regulator of brown adipose mitochondrial bioenergetics will be of significance across several fields. That said, a few areas of concern were apparent. Concerns are detailed in the "Major" and "Minor" comments section below. Additional experiments do not appear to be required, assuming the authors adequately acknowledge the limitations of the study and either remove or qualify speculative claims.

Major Comments:

• The authors convincingly demonstrate that IF1 expression is specifically down-regulated in BAT upon cold-exposure. These data strongly implicate a role for IF1 in BAT bioenergetics, a major claim of the authors and a novel finding herein. Additional major strengths of the paper, which provide excellent scientific rigor include the use of both loss of function and gain of function approaches for IF1. In addition, the mutant IF1 experiments are excellent, as they convincingly show that the effects of IF1 are dependent on its ability to bind CV.
• Regarding Figure 1 - Did the content of ATP synthase change? In figure 1A-B, the authors show that ATPase activity of CV is higher in cold-adapted mice. While this result could be due to a loss of IF1, it could also be due to a higher expression of CV. To control for this, the authors should consider blotting for CV, which would allow for ATPase activity to be normalized to expression.
• Regarding MMP generated specifically by ATP hydrolysis at CV, the reversal potential for ANT occurs at a more negative MMP than that of CV (PMID: 21486564). Because reverse transport of ATP (cytosol to matrix) via ANT will also generate a MMP, it is speculative to state that the MMP in the assay is driven by ATP hydrolysis at CV. It is possible and maybe even likely that the majority of the MMP is driven by ANT flux, which in turn limits the amount of ATP hydrolyzed by CV. Admittedly, it is very challenging to different MMP from ANT vs that from CV, thus the authors simply need to acknowledge that the specific contribution of ATP hydrolysis to MMP remains to be fully determined. That said, the fact that ATP-dependent MMP tracks with IF1 expression does certainly implicate a role for ATP hydrolysis in the process. The authors should consider including a discussion of the ambiguity of the assay to avoid confusion. A role for ANT likely should be incorporated in the Fig. 1J cartoon.
• Regarding the lack of effect of IF1 silencing on MMP, it is possible that IF1 total protein levels are simply lower in cultured brown fat cells relative to tissue? The authors could consider testing this by blotting for IF1 and CV in BAT and brown fat cells. The ratio of IF1/ATP5A1 in tissue versus cells may provide some amount of mechanistic evidence as to their findings.
• The calculation of ATP synthesis from respiration sensitive to oligomycin has many conceptual flaws. Unlike glycolysis, where ATP is produced via substrate level phosphorylation, during OXPHOS, the stoichiometry of ATP produced per 2e transfer is not known in intact brown adipose cells. This is a major limitation of this "calculated ATP synthesis" approach that is beginning to become common. Such claims are speculative and thus likely do more harm than good. In addition to ANT and CV, there are many proton-consuming reactions driven by the proton motive force (e.g., metabolite transport, Ca2+ cycling, NADPH synthesis). Although it remains unclear how much proton conductance is diverted to non ATP synthesis dependent processes, it seems highly likely that these processes contribute to respiratory demand inside living cells. Moreover, just as occurs with UCP1 in response to adrenergic stimuli, proton conductance across the various proton-dependent processes likely changes depending on the cellular context, which is another reason why using a fixed stoichiometry to calculate how much ATP is produced from oxygen consumption is so highly flawed. Maximal P/O values that are often used for NAD/FAD linked flux are generated using experimental conditions that favor near complete flux through the ATP synthesis system (supraphysiological substrate and ADP levels). The true P/O value inside living cells is likely to be lower.
• Why are the results in Figure 3K expressed as a % of basal? Could the authors please normalize the OCR data to protein and/or provide a justification for why different normalization strategies were used between 3K and 3M?
• The authors claim that IF1 overexpression lowers ATP production via OXPHOS. However, given the major limitations of this assay (ass discussed above), these claims should be viewed as speculation. This needs to be addressed by the authors as a major limitation. The fact that the ATP/ADP levels did not change do not support of reduction in ATP production, as claimed in the title of Figure 4.
• In the discussion, the authors state "However, considering that IF1 inhibits F1-ATP synthase in a 1:1 stoichiometric ratio, the relatively higher expression of IF1 in BAT at room temperature could represent an additional inhibitory factor for ATP synthesis in this tissue." This does not appear to be correct. Although IF1 has been suggested to partially lower maximal rates of ATP synthesis rates, most of this evidence comes from over-expression experiments. According to the current understanding of IF1-CV interaction, the protein is expelled from the complex during rotation in favor of ATP synthesis (PMID: 37002198). It is far more likely that ATP synthesis is low in BAT mitochondria due to the low CV expression. Relative to heart and when normalized to mitochondrial content, CV expression in BAT mitochondria is about 10% that of heart (PMID: 33077793).
• The last sentence of the manuscript states, "Given the importance of IF1 to control brown adipocyte energy metabolism, lowering IF1 levels therapeutically might enhance approaches to enhance NST for improving cardiometabolic health in humans." This sentence seems at odds with the evidence that IF1 levels go up, not down, in human BAT upon cold exposure.

Minor Comments:

• The term "anaerobic glycolysis" is used throughout. All experiments were performed under normoxic conditions, thus the correct term is "aerobic glycolysis.
• Only male mice were used in the study, could the authors please provide a justification for this?

Significance

Overall, the quality of the work is very high. Given that IF1 is implicated across many fields of study, the novel discovery of IF1 as a regulator of brown adipose mitochondrial bioenergetics will be of significance across several fields.

My expertise is in mitochondrial thermodynamics; thus, I do not feel there are any parts of the paper that I do not have sufficient expertise to evaluate.

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Reply to the reviewers

Manuscript number: RC-2023-02218R

Corresponding author(s): Steven, McMahon

1. General Statements [optional]

*We were pleased to receive the encouraging critiques and very much appreciate the Reviewer's specific comments and suggestions. In this revised version of our manuscript, we have made a number of substantive additions and modifications in response to these comments/suggestions. We hope you agree that the study is now improved to the point where it is suitable for publication. *

2. Point-by-point description of the revisions

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

Summary This study describes efforts to characterize differences in the roles of the two related human decapping factors Dcp1a and Dcp1b by assessing mRNA decay and protein associations in knockdown and knockout cell lines. The authors conclude that these proteins are non-redundant based on the observations that loss of DCp1a versus Dcp1b impacts the decapping complex (interactome) and the transcriptome differentially.

Major comments • While the experiments appear to be well designed and executed and the data of generally high quality, the conclusions are drawn without sufficient consideration for the fact that these two proteins form a heterotrimeric complex. The authors assume that there are distinct homotrimeric complexes rather than a single complex with both proteins in. Homotrimers may have new/different functions not normally seen when both proteins are expressed. Thus while it is acceptable to infer that the functions of these two proteins within the decapping complex are distinct, it is not clear that they act separately, or that complexes naturally exist without one or the other. A careful evaluation of the relative ratios of Dcp1a and b overall and in decapping complexes would be informative if the authors want to make stronger statements about the roles of these two factors.

RESPONSE: Thank you for this valuable comment. We have substantially edited the manuscript to incorporate these points. Examples include a detailed analysis of iBAQ values for the DDX6, DCP1a, and DCP1b interactomes (which now allows us to estimate the ratios of DCP1a and DCP1b in these complexes) and cellular fractionation to interrogate complex integrity (using Superose 6).

• The concept of buffering is not adequately introduced and the interpretation of observations that RNAs with increased half life do not show increased protein abundance - that Dcp1a/b are involved in transcript buffering is nebulous. In order to support this interpretation, the mRNA abundances (NOT protein abundances) should be assessed, and even then, there is no way to rule out indirect effects. RESPONSE: Thank you for this comment. In the revised version of the manuscript, we introduced the concept of transcript buffering at an earlier stage as one of the potential explanations for our findings. We were also able to use a new algorithm (grandR) to estimate half-lives and synthesis rates from our data. These new data add strength to the argument that DCP1a and DCP1b are linked to transcript buffering pathways.

• It might be interesting to see what happens when both factors are depleted to get an idea of the overall importance of each one.

RESPONSE: In our work we tried to emphasize the differences between the two paralogs. We believe that doing double knockout or knockdown would mask the distinct impacts of the paralogs. In data not included in this study, we have shown that cells lacking both DCP1a and DCP1b are viable. We did check PARP cleavage in the CRISPR generated cell pools of DCP1a KO, DCP1b KO, and the double KO. The WB measuring the PARP cleavage is shown in the supplemental material (Supplementary Material: Replicates)

• The algorithms etc used for data analysis should be included at the time of publication. Version number and settings used for SMART to define protein domains, and webgestalt should be indicated

RESPONSE: We apologize for this oversight. Version number and settings used for the webtools (SMART, Webgestalt) are now included. The analysis pipeline for half-lives and synthesis rates estimation as well as all the files and the code needed to generate the figures in the paper are available on zenodo (https://zenodo.org/records/10725429).

• Statistical analysis is not provided for the IP experiments, the number of replicates performed is not indicated and quantification of KD efficiency are not provided.

RESPONSE: The number of replicates performed in each experiment is now clearly indicated and quantifications of knockdown efficiency are provided (Supplemental Figure 3A and 3B, Figure 3A, Figure 3B).

• The possibility that the IP Antibody interferes with protein-protein interactions is not mentioned.

RESPONSE: Thank you for this comment. The revised manuscript includes a discussion of the antibody epitope location and the potential for impact on protein-protein interactions.

Minor comments • P4 - "This translational repression of mRNA associated with decapping can be reversed, providing another point at which gene expression can be regulated (21)" - implies that decapping can be reversed or that decapped RNAs are translated. I don't think this is technically true.

RESPONSE: There have been several studies that document the reversal of decapping. These findings are summarized in the following reviews.

Schoenberg, D. R., & Maquat, L. E. (2009). Re-capping the message. Trends in biochemical sciences, 34(9), 435-442.

Trotman, J. B., & Schoenberg, D. R. (2019). A recap of RNA recapping. Wiley Interdisciplinary Reviews: RNA, 10(1), e1504.

• P11 - how common is it for higher eukaryotes to have 2 DCP genes? *RESPONSE: Metazoans have 2 DCP1 genes. *

• Fig S1 - says "mammalian tissues" in the text but the data is all human. The statement that "expression analyses revealed that DCP1a and DCP1b have concordant rather than reciprocal expression patterns across different mammalian tissues (Supplemental Figure 1)" is a bit misleading as no evidence for correlation or anti-correlation is provided. Also co-expression is not strong support for the idea that these genes have non-redundant functions. Both genes are just expressed in all tissues - there's no evidence provided that they are concordantly expressed. In bone marrow it may be worth noting that one is high and the other low - i.e. reciprocal. *RESPONSE: We appreciate this comment. We have corrected the interpretation of the aforementioned dataset. We have also incorporated a more detailed discussion in the text of the paper. As the Reviewer pointed out, there are a subset of tissues where their expression appears to be reciprocal. *

• Fig 1A - it is not clear what the different colors mean. Does Sc DCP1 have 1 larger EVH or 2 distinct ones. Are the low complexity regions in Sc DCP2 the SLiMs. *RESPONSE: Thank you for this comment. We have corrected this ambiguity to reflect that Sc DCP1 has one EVH1 domain that is interconnected by a flexible hinge. The low-complexity regions typically contain short linear motifs (SLIMs), however, not all low-complexity regions have been verified to contain them. In the figure, only low-complexity regions are shown. The text of the paper refers only to verified SLIMs . *

• P11 - why were HCT116 cells selected? RESPONSE: HCT116 cells are an easily transfectable human cell line and have been widely used in biochemical and molecular studies, including studies of mRNA decapping (see references below). Since decapping is impacted by viral proteins we avoided the use of other commonly used cell models such as HEK293T or HeLa.

https://pubmed.ncbi.nlm.nih.gov/?term=decapping+hct116&sort=date&size=200

• Fig 1B - what are the asterisks by the RNA names? Might be worth noting that over-expression of DCP1b reduced IP of DCP1a. There's no quantification and no indication of the number of times this experiment was repeated. Data from replicates and quantification of the knockdown efficiency in each replicate would be nice to see. *RESPONSE: Thank you for this comment. Asterisks indicate that those bands were from a second gel, as DCP1a and DCP1b run at approximately the same molecular weight. We have now included a note in our figure legend to indicate this. The knockdown efficiency is provided (Figure 3 and Supplemental Figure 3). We also noted the number of replicas for each IP in figure 1. The replicas are provided as supplementary material (Supplementary Materials: Replicates). *

• Fig 1C/1D - why are there 3 bands in the DCP1a blot? Quantification of the IP bands is necessary to say whether there is an effect or not of over-expression/KO. RESPONSE: The additional bands in DCP1a blots are background. When we stained the whole blot for DCP1a, in cells which with complete DCP1a KO cells (clone A3), these bands still appear (Supplementary Material: Validation of the KO clones). Quantifications of the bands in the overexpression experiments is now provided.

• Fig 3 - is it possible that differences are due to epitope positions for the antibodies used for IP? RESPONSE: We do not believe so. DCP1a antibody binds roughly 300-400 residues on DCP1a, and DCP1b antibody binds around Val202. Antibodies therefore do not bind DCP1a or DCP1b low-complexity regions (which are largely responsible for interacting with the decapping complex interactome). Antibodies don't bind the EVH1 domains or the trimerization domain, which are needed for their interaction with DCP2 and each other.

• Fig 5A - the legend doesn't match the colors in the figure. It is not clear how the pRESPONSE: Thank you for this comment. We have corrected this issue in the revised version of the paper. High-confidence proteins are those with pRESPONSE: Thank you for this comment. We have corrected this issue in the revised version of the paper.*

• There are a few more recent studies on buffering that should be cited and more discussion of this in the introduction is necessary if conclusions are going to be drawn about buffering. *RESPONSE: We have included a discussion of transcript buffering in the introduction. *

• The heatmaps in figure 2 are hard to interpret. RESPONSE: To clarify the heatmaps, we included a more detailed description in the figure legends, have enlarged the heatmaps themselves, and have added more extensive labeling.

Reviewer #1 (Significance (Required)):

• Strengths: The experiments appear to be done well and the datasets should be useful for the field. • Limitations: The results are overinterpreted - different genes are affected by knocking down one or other of these two similar proteins but this does not really tell us all that much about how the two proteins are functioning in a cell where both are expressed. • Audience: This study will appeal most to a specialized audience consisting of those interested in the basic mechanisms of mRNA decay. Others may find the dataset useful. • This study might complement and/or be informed by another recent study in BioRXiv - https://doi.org/10.1101/2023.09.04.556219 • My field of expertise is mRNA decay - I am qualified to evaluate the findings within the context of this field. I do not have much experience of LC-MS-MS and therefore cannot evaluate the methods/analysis of this part of the study.

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

The authors provide evidence that Dcp1a and Dcp1b - two paralogous proteins of the mRNA decapping complex - may have divergent functions in a cancer cell line. In the first part, the authors show that interaction of Dcp2 with EDC4 is diminished upon depletion of Dcp1a but not affected by depletion of Dcp1b. The results have been controlled by overexpression of Dcp1b as it may be limiting factor (i.e. expression levels too low to compensate for depletion of Dcp1a reduced interaction with EDC3/4 while depletion of Dcp1b lead to opposite and increase interactions). They then defined the protein interactome of DDX6 in parental and Dcp1a or Dcp1b depleted cells. Here, the authors show some differential association with EDC4 again, which is along results shown in the first part. The authors further performed SLAM-seq and identified subsets of mRNA whose decay rates are common but also different upon depletion with Dcp1a and Dcp1b. Interestingly, it seems that Dcp1a preferentially targets mRNAs for proteins regulating lymphocyte differentiation. To further test whether changes in RNA decay rates are also reflected at the protein levels, they finally performed an MS analysis with Dcp1a/b depleted cells. However no significant overlap with mRNAs showing altered stability could be observed; and the authors suggested that the lack of congruence reflects translational repression.

Major comments: 1. While functional difference between Dcp1a and Dcp1b are interesting and likely true, there are overinterpretations that need correction or further evidence for support. Sentences like "DCP1a regulates RNA cap binding proteins association with the decapping complex and DCP1b controls translational initiation factors interactions (Figure 2E)" sound misleading. While differential association with proteins has been recognised with MS-data, it does not necessary implement an active process of control/regulation. To make the claim on 'control/regulation', and inducible system or introduction of mutants would be required.

RESPONSE: This set of comments were particularly useful in helping us refine the presentation of our findings. We have edited our manuscript to be more specific about the limits of our data.

1. The MS analysis is not clearly described in the text and it is unclear how authors selected high-confident proteins. The reader needs to consider the supplemental tables to find out what controls were used. Furthermore, the authors should show correlation plots of MS data between replicates. For instance, there seems to be limited correlation among some of the replicates (e.g. Dcp1b_ko3 sample, Fig. 2c). Any explanation in this variance?

*RESPONSE: We have now included a clear description of how all high-confidence proteins were selected in the Methods and Results sections. The revised manuscript also includes a more thorough description of the controls used and the number of replicates for individual experiments. The PCA plots have now been included where appropriate. The variance in this sample is likely technical. *

1. GO analysis for the proteome analysis should consider the proteome and not the genome as the background. The authors should also indicate the corrected P-values (multiple testing) FDRs.

*RESPONSE: Webgestalt uses a reference set of IDs to recognize the input IDs, and it does not use it for the background analysis in the classical sense. We repeated a subset of our proteome analyses using the 'genome-protein coding' as background and obtained the same result as in our original analysis. All ontology analyses now include raw p-values and/or FDRs when appropriate. *

1. Fig 2E. The figures display GO enrichments needs better explanation and additional data can be added. The enrichment ratio is not explained (is this normalised?) and p-values and FDRs, number of proteins in respective GO category should be added. *RESPONSE: More thorough explanations of the GO enrichments are now included. The supplemental data contains all p-values (raw and adjusted), as well as the number of proteins in each GO category. The Enrichment ratio is normalized and contains information about the number of proteins that are redundant in multiple groups. GO Ontology analyses are now displayed with p-values and/or FDR values, and in this case the enrichment ratio contains information regarding the number of proteins found in our input set and the number of expected proteins in the GO group. The network analysis shows the FDR values and the number of proteins found in the groups compared. *

Minor: 5. These studies were performed in a colorectal carcinoma cell line (HCT116). The authors should justify the choice of this specialised cell line. Furthermore, one wonders whether similar conclusions can be drawn with other cell lines or whether findings are specific to this cancer line.

RESPONSE: The study that is currently in pre-print in BioRxiv (https://doi.org/10.1101/2023.09.04.556219*) utilized HEK293Ts and found similar results to ours when examining the various relationships between the core decapping core members. *

1. Fig. 1B. It is unclear what DCP1b* refers to? There are bands of different size that are not mentioned by the authors - are those protein isoforms or what are those referring to? A molecular marker should be added to each Blots. Uncropped Western images and markers should be provided in the Supplement. *RESPONSE: The asterisk indicates that these images came from a second western blot gel (DCP1a and DCP1b have a similar molecular weight and cannot be probed on the same membrane). Uncropped western blot images and markers (as available) are provided in the supplement. *

2. MS data submitted to public repository with access. No. indicated in the manuscript.

RESPONSE: MS data is submitted as supplementary datasets to the paper. It contains the analyzed data as well as the LCMSMS output. We are in the process of submitting the raw LSMSMS data to a public repository.

Fig 3. A Venn Diagram displaying the overlap of identified proteins should be added. GO analysis should be done considering the proteome as background (as mentioned above).

*RESPONSE: A Venn diagram showing the overlap among the proteins identified is now included in the revised version. *

Reviewer #2 (Significance (Required)):

Overall, this is a large-scale integrative -omics study that suggest functional difference between Dcp1 paralogues. While it seems clear that both paralogous have some different functions and impact, there are overinterpretations in place and further evidence would to be provided to substantiate conclusions made in the paper. For instance, while the interactions with Dcp2/Ddx6 in the absence of Dcp1a,b with EDC4/3 may be altered (Fig. 1, 2), the functional implications of this changed associations remains unresolved and not further discussed. As such, it remains somehow disconnected with the following experiments and compromises the flow of the study. The observed differences in decay-rates for distinct functionally related sets of mRNAs is interesting; however, it remains unclear whether those are direct or rather indirect effects. This is further obscured by the absence of any correlation to changes in protein levels, which the authors interpreted as 'transcriptional buffering'. In this regard, it is puzzling how the authors can make a statement about transcriptional buffering? While this may be an interesting aspect and concept of the discussion, there is no primary data showing such a functional impact.

As such, the study is interesting as it claims functional differences between DCP1a/b paralogous in a cancer cell line. Nevertheless, I am not sure how trustful the MS analysis and decay measurements are as there is not further validation. It woudl be interesting if the authors could go a bit further and draw some hypothesis how the selectivty could be achieved i.e interaction with RNA-binding proteins that may add some specificity towards the target RNAs for differential decay. As such, the study remains unfortunately rather descriptive without further functional insight.

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

Review on "Non-redundant roles for the human mRNA decapping cofactor paralogs DCP1a and DCP1b" by Steven McMahon and co-workers mRNA decay is a critical step in the regulation of gene expression. In eukaryotes, mRNA turnover typically begins with the removal of the poly(A) tail, followed by either removal of the 5' cap structure or exonucleolytic 3'-5' decay catalyzed by the exosome. The decapping enzyme DCP2 forms a complex with its co-activator DCP1, which enhances decapping activity. Mammals are equipped with two DCP1 paralogs, namely DCP1a and DCP1b. Metazoans' decapping complexes feature additional components, such as enhancer of decapping 4 (EDC4), which supports the interaction between DCP1 and DCP2, thereby amplifying the efficiency of decapping. This work focuses on DCP1a and DCP1b and investigates their distinct functions. Using DCP1a- and DCP1a-specific knockdowns as well as K.O. cell lines, the authors find surprising differences between the DCP1 paralogs. While DCP1a is essential for the assembly of EDC4-containig decapping complexes and interactions with mRNA cap binding proteins, DCP1b mediates interactions with the translational machinery. Furthermore, DCP1a and DCP1b target different mRNAs for degradation, indicating that they execute non-overlapping functions. The findings reported here expand our understanding of mRNA decapping in human cells, shedding light on the unique contributions of DCP1a and DCP1b to mRNA metabolism. The manuscript tackles an interesting subject. Historically, the emphasis has been on studying DCP1a, while DCP1b has been deemed a functionally redundant homolog of DCP1a. Therefore, it is commendable that the authors have taken on this topic and, with the help of knockout cell lines, aimed to dissect the function of DCP1a and DCP1b. Despite recognizing the significance of the subject and approach, the manuscript falls short of persuading me. Following a promising start in Figure 1 (which still has room for improvement), there is a distinct decline in overall quality, with only relatively standard analyses being conducted. However, I do not want to give the authors a detailed advice on maximizing the potential of their data and presenting it convincingly. So, here are just a few key points for improvement: Figure 1C: Upon closer examination, a faint band is still visible at the size of DCP1a in the DCP1a knockout cells. Could this be leaky expression of DCP1a? The authors should provide an in-depth characterization of their cells (possibly as supplementary material), including identification of genomic changes (e.g. by sequencing of the locus) and Western blots with longer exposure, etc.

*RESPONSE: Thank you for this comment. The in-depth characterization of our cells is now included in the Supplementary Material. DCP1a KO cells and DCP1b KO cells indicated as single cell clones have been confirmed to have no DCP1a or DCP1b expression. In Figure 1D and Figure 3, polyclonal pool cells were used as indicated (only for DCP1a KO). *

Figure 2: It is great to see that the effects of the KOs are also visible in the DDX6 immunoprecipitation. However, I wonder if the IP clearly confirms that the KO cells indeed do not express DCP1a or DCP1b. In the heatmap in Figure 2B, it appears as if the proteins are only reduced by a log2-fold change of approximately 1.5? Additionally, Figure 2 shows a problem that persists in the subsequent figures. The visual presentation is not particularly appealing, and essential details, such as the scale of the heatmap in 2B (is it log2 fold?), are lacking.

*RESPONSE: The in-depth characterization of our cells is included in the Supplementary Materials and confirms the presence of single-cell clones where indicated. As noted above, only Figure 1D and Figure 3 used DCP1a KO pooled cells. The heatmap in Figure 2B is scaled by row using the pheatfunction in R studio. The actual data for the heatmap comes from protein intensities from the LC-MS/MS analysis. We have improved the visual presentation in the revised manuscript. *

Figure 3: I wonder why there are no primary data shown here, only processed GO analyses. Wouldn't one expect that DCP2 interacts mainly with DCP1a, but less with DCP1b? Is this visible in the data? Moreover, such analyses are rather uninformative (as reflected in the GO terms themselves, for instance, "oxoglutarate dehydrogenase complex" doesn't provide much meaningful insight). The authors should rather try to derive functional and mechanistic insights from their data.

RESPONSE: We have now revised this Figure to include primary data as well as the IP of DCP1a in DCP1b KO cells (single cell clones) and the IP of DCP1b in DCP1a KO cells (pooled cells). We identified EDC3 in the high-confidence protein pool. The EDC3:DCP1a interaction is enhanced in DCP1b KO cells. We also found that the EDC3:DCP1b interaction is less abundant in DCP1a KO cells. This is consistent with our data in Figures 1 and 2. DCP2 was not identified in the interactomes of either DCP1a or DCP1b. This is not unusual as DCP2 is highly flexible and the association between DCP1s with DCP2 is transient and facilitated by other proteins.

In Fig. 4 the potential of the approach is not fully exploited. Firstly, I would advocate for omitting the GO analyses, as, in my opinion, they offer little insight. Again, crucial information is missing to assess the results. While 75 nt reads are mentioned in the methods, the sequencing depth remains unspecified. Figure 4b should be included in the supplements. Furthermore, I strongly recommend concentrating on insights into the mechanisms of DCP1a and DCP1b-containing complexes. E.g. what characteristics distinguish DCP1a and DCP1b-dependent mRNAs? Are these targets inherently unstable? Why are they degraded? Are they known decapping substrates?

*RESPONSE: Thank you for this comment. We have now revised this figure and have included information about sequencing depth and other pertinent information. We have been able to use a newly available algorithm (grandR) and were able to estimate half-lives and synthesis rates. This is a significant addition to the paper. We were also able to compare significantly impacted mRNAs (by DCP1a or DCP1b loss) to the established DCP2 target list. *

In general, I suggest the authors revise the manuscript with a focus on the potential readers. Reduce Gene Ontology (GO) analyses and heatmaps, and instead, incorporate more analyses regarding the molecular processes associated with the different decapping complexes.

*RESPONSE: We removed selected GO analyses and heatmaps from the main body of the manuscript (included as Supplementary Figures instead). For our LC-MS/MS datasets, we added iBAQ analyses of the DDX6 IP, DCP1a IP, and DCP1b IP in the control conditions. Cellular fractionation studies (using Superose 6 chromatography) were also added to the paper and allow us to interrogate decapping complex composition in more detail. The revised version of the manuscript includes a new 4SU labeling experiment (pulse-chase) as well as estimation of half-lives and synthesis rates in our conditions. Also included is relevant information about DCP1b transcriptional regulation. *

Reviewer #3 (Significance (Required)):

The manuscript in its current form could benefit from substantial revisions for it to be considered impactful for researchers in the field.

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Referee #3

Evidence, reproducibility and clarity

Review on "Non-redundant roles for the human mRNA decapping cofactor paralogs DCP1a and DCP1b" by Steven McMahon and co-workers

mRNA decay is a critical step in the regulation of gene expression. In eukaryotes, mRNA turnover typically begins with the removal of the poly(A) tail, followed by either removal of the 5' cap structure or exonucleolytic 3'-5' decay catalyzed by the exosome. The decapping enzyme DCP2 forms a complex with its co-activator DCP1, which enhances decapping activity. Mammals are equipped with two DCP1 paralogs, namely DCP1a and DCP1b. Metazoans' decapping complexes feature additional components, such as enhancer of decapping 4 (EDC4), which supports the interaction between DCP1 and DCP2, thereby amplifying the efficiency of decapping.

This work focuses on DCP1a and DCP1b and investigates their distinct functions. Using DCP1a- and DCP1a-specific knockdowns as well as K.O. cell lines, the authors find surprising differences between the DCP1 paralogs. While DCP1a is essential for the assembly of EDC4-containig decapping complexes and interactions with mRNA cap binding proteins, DCP1b mediates interactions with the translational machinery. Furthermore, DCP1a and DCP1b target different mRNAs for degradation, indicating that they execute non-overlapping functions.

The findings reported here expand our understanding of mRNA decapping in human cells, shedding light on the unique contributions of DCP1a and DCP1b to mRNA metabolism. The manuscript tackles an interesting subject. Historically, the emphasis has been on studying DCP1a, while DCP1b has been deemed a functionally redundant homolog of DCP1a. Therefore, it is commendable that the authors have taken on this topic and, with the help of knockout cell lines, aimed to dissect the function of DCP1a and DCP1b.

Despite recognizing the significance of the subject and approach, the manuscript falls short of persuading me. Following a promising start in Figure 1 (which still has room for improvement), there is a distinct decline in overall quality, with only relatively standard analyses being conducted. However, I do not want to give the authors a detailed advice on maximizing the potential of their data and presenting it convincingly. So, here are just a few key points for improvement:

Figure 1C: Upon closer examination, a faint band is still visible at the size of DCP1a in the DCP1a knockout cells. Could this be leaky expression of DCP1a? The authors should provide an in-depth characterization of their cells (possibly as supplementary material), including identification of genomic changes (e.g. by sequencing of the locus) and Western blots with longer exposure, etc.

Figure 2: It is great to see that the effects of the KOs are also visible in the DDX6 immunoprecipitation. However, I wonder if the IP clearly confirms that the KO cells indeed do not express DCP1a or DCP1b. In the heatmap in Figure 2B, it appears as if the proteins are only reduced by a log2-fold change of approximately 1.5? Additionally, Figure 2 shows a problem that persists in the subsequent figures. The visual presentation is not particularly appealing, and essential details, such as the scale of the heatmap in 2B (is it log2 fold?), are lacking.

Figure 3: I wonder why there are no primary data shown here, only processed GO analyses. Wouldn't one expect that DCP2 interacts mainly with DCP1a, but less with DCP1b? Is this visible in the data? Moreover, such analyses are rather uninformative (as reflected in the GO terms themselves, for instance, "oxoglutarate dehydrogenase complex" doesn't provide much meaningful insight). The authors should rather try to derive functional and mechanistic insights from their data.

In Fig. 4 the potential of the approach is not fully exploited. Firstly, I would advocate for omitting the GO analyses, as, in my opinion, they offer little insight. Again, crucial information is missing to assess the results. While 75 nt reads are mentioned in the methods, the sequencing depth remains unspecified. Figure 4b should be included in the supplements. Furthermore, I strongly recommend concentrating on insights into the mechanisms of DCP1a and DCP1b-containing complexes. E.g. what characteristics distinguish DCP1a and DCP1b-dependent mRNAs? Are these targets inherently unstable? Why are they degraded? Are they known decapping substrates?

In general, I suggest the authors revise the manuscript with a focus on the potential readers. Reduce Gene Ontology (GO) analyses and heatmaps, and instead, incorporate more analyses regarding the molecular processes associated with the different decapping complexes.

Significance

The manuscript in its current form could benefit from substantial revisions for it to be considered impactful for researchers in the field.

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Referee #2

Evidence, reproducibility and clarity

The authors provide evidence that Dcp1a and Dcp1b - two paralogous proteins of the mRNA decapping complex - may have divergent functions in a cancer cell line. In the first part, the authors show that interaction of Dcp2 with EDC4 is diminished upon depletion of Dcp1a but not affected by depletion of Dcp1b. The results have been controlled by overexpression of Dcp1b as it may be limiting factor (i.e. expression levels too low to compensate for depletion of Dcp1a reduced interaction with EDC3/4 while depletion of Dcp1b lead to opposite and increase interactions). They then defined the protein interactome of DDX6 in parental and Dcp1a or Dcp1b depleted cells. Here, the authors show some differential association with EDC4 again, which is along results shown in the first part. The authors further performed SLAM-seq and identified subsets of mRNA whose decay rates are common but also different upon depletion with Dcp1a and Dcp1b. Interestingly, it seems that Dcp1a preferentially targets mRNAs for proteins regulating lymphocyte differentiation. To further test whether changes in RNA decay rates are also reflected at the protein levels, they finally performed an MS analysis with Dcp1a/b depleted cells. However no significant overlap with mRNAs showing altered stability could be observed; and the authors suggested that the lack of congruence reflects translational repression.

Major comments:

1. While functional difference between Dcp1a and Dcp1b are interesting and likely true, there are overinterpretations that need correction or further evidence for support. Sentences like "DCP1a regulates RNA cap binding proteins association with the decapping complex and DCP1b controls translational initiation factors interactions (Figure 2E)" sound misleading. While differential association with proteins has been recognised with MS-data, it does not necessary implement an active process of control/regulation. To make the claim on 'control/regulation', and inducible system or introduction of mutants would be required.
2. The MS analysis is not clearly described in the text and it is unclear how authors selected high-confident proteins. The reader needs to consider the supplemental tables to find out what controls were used. Furthermore, the authors should show correlation plots of MS data between replicates. For instance, there seems to be limited correlation among some of the replicates (e.g. Dcp1b_ko3 sample, Fig. 2c). Any explanation in this variance?
3. GO analysis for the proteome analysis should consider the proteome and not the genome as the background. The authors should also indicate the corrected P-values (multiple testing) FDRs.
4. Fig 2E. The figures display GO enrichments needs better explanation and additional data can be added. The enrichment ratio is not explained (is this normalised?) and p-values and FDRs, number of proteins in respective GO category should be added.

Minor:

1. These studies were performed in a colorectal carcinoma cell line (HCT116). The authors should justify the choice of this specialised cell line. Furthermore, one wonders whether similar conclusions can be drawn with other cell lines or whether findings are specific to this cancer line.
2. Fig. 1B. It is unclear what DCP1b* refers to? There are bands of different size that are not mentioned by the authors - are those protein isoforms or what are those referring to? A molecular marker should be added to each Blots. Uncropped Western images and markers should be provided in the Supplement.
3. MS data submitted to public repository with access. No. indicated in the manuscript.
4. Fig 3. A Venn Diagram displaying the overlap of identified proteins should be added. GO analysis should be done considering the proteome as background (as mentioned above).

Significance

Overall, this is a large-scale integrative -omics study that suggest functional difference between Dcp1 paralogues. While it seems clear that both paralogous have some different functions and impact, there are overinterpretations in place and further evidence would to be provided to substantiate conclusions made in the paper. For instance, while the interactions with Dcp2/Ddx6 in the absence of Dcp1a,b with EDC4/3 may be altered (Fig. 1, 2), the functional implications of this changed associations remains unresolved and not further discussed. As such, it remains somehow disconnected with the following experiments and compromises the flow of the study. The observed differences in decay-rates for distinct functionally related sets of mRNAs is interesting; however, it remains unclear whether those are direct or rather indirect effects. This is further obscured by the absence of any correlation to changes in protein levels, which the authors interpreted as 'transcriptional buffering'. In this regard, it is puzzling how the authors can make a statement about transcriptional buffering? While this may be an interesting aspect and concept of the discussion, there is no primary data showing such a functional impact.

As such, the study is interesting as it claims functional differences between DCP1a/b paralogous in a cancer cell line. Nevertheless, I am not sure how trustful the MS analysis and decay measurements are as there is not further validation. It woudl be interesting if the authors could go a bit further and draw some hypothesis how the selectivty could be achieved i.e interaction with RNA-binding proteins that may add some specificity towards the target RNAs for differential decay. As such, the study remains unfortunately rather descriptive without further functional insight.

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Referee #1

Evidence, reproducibility and clarity

Summary

This study describes efforts to characterize differences in the roles of the two related human decapping factors Dcp1a and Dcp1b by assessing mRNA decay and protein associations in knockdown and knockout cell lines. The authors conclude that these proteins are non-redundant based on the observations that loss of DCp1a versus Dcp1b impacts the decapping complex (interactome) and the transcriptome differentially.

Major comments

• While the experiments appear to be well designed and executed and the data of generally high quality, the conclusions are drawn without sufficient consideration for the fact that these two proteins form a heterotrimeric complex. The authors assume that there are distinct homotrimeric complexes rather than a single complex with both proteins in. Homotrimers may have new/different functions not normally seen when both proteins are expressed. Thus while it is acceptable to infer that the functions of these two proteins within the decapping complex are distinct, it is not clear that they act separately, or that complexes naturally exist without one or the other. A careful evaluation of the relative ratios of Dcp1a and b overall and in decapping complexes would be informative if the authors want to make stronger statements about the roles of these two factors.
• The concept of buffering is not adequately introduced and the interpretation of observations that RNAs with increased half life do not show increased protein abundance - that Dcp1a/b are involved in transcript buffering is nebulous. In order to support this interpretation, the mRNA abundances (NOT protein abundances) should be assessed, and even then, there is no way to rule out indirect effects.
• It might be interesting to see what happens when both factors are depleted to get an idea of the overall importance of each one.
• The algorithms etc used for data analysis should be included at the time of publication. Version number and settings used for SMART to define protein domains, and webgestalt should be indicated
• Statistical analysis is not provided for the IP experiments, the number of replicates performed is not indicated and quantification of KD efficiency are not provided.
• The possibility that the IP Antibody interferes with protein-protein interactions is not mentioned.

Minor comments - P4 - "This translational repression of mRNA associated with decapping can be reversed, providing another point at which gene expression can be regulated (21)" - implies that decapping can be reversed or that decapped RNAs are translated. I don't think this is technically true. - P11 - how common is it for higher eukaryotes to have 2 DCP genes?<br /> - Fig S1 - says "mammalian tissues" in the text but the data is all human. The statement that "expression analyses revealed that DCP1a and DCP1b have concordant rather than reciprocal expression patterns across different mammalian tissues (Supplemental Figure 1)" is a bit misleading as no evidence for correlation or anti-correlation is provided. Also co-expression is not strong support for the idea that these genes have non-redundant functions. Both genes are just expressed in all tissues - there's no evidence provided that they are concordantly expressed. In bone marrow it may be worth noting that one is high and the other low - i.e. reciprocal. - Fig 1A - it is not clear what the different colors mean. Does Sc DCP1 have 1 larger EVH or 2 distinct ones. Are the low complexity regions in Sc DCP2 the SLiMs.<br /> - P11 - why were HCT116 cells selected? - Fig 1B - what are the asterisks by the RNA names? Might be worth noting that over-expression of DCP1b reduced IP of DCP1a. There's no quantification and no indication of the number of times this experiment was repeated. Data from replicates and quantification of the knockdown efficiency in each replicate would be nice to see. - Fig 1C/1D - why are there 3 bands in the DCP1a blot? Quantification of the IP bands is necessary to say whether there is an effect or not of over-expression/KO. - Fig 3 - is it possible that differences are due to epitope positions for the antibodies used for IP? - Fig 5A - the legend doesn't match the colors in the figure. It is not clear how the p<0.05 high confident genes are identified - only some of the genes with p<0.05 are colored red. - Fig 5E and F - x-axis should be log2 fold change - There are a few more recent studies on buffering that should be cited and more discussion of this in the introduction is necessary if conclusions are going to be drawn about buffering. - The heatmaps in figure 2 are hard to interpret.

Significance

• Strengths: The experiments appear to be done well and the datasets should be useful for the field.
• Limitations: The results are overinterpreted - different genes are affected by knocking down one or other of these two similar proteins but this does not really tell us all that much about how the two proteins are functioning in a cell where both are expressed.
• Audience: This study will appeal most to a specialized audience consisting of those interested in the basic mechanisms of mRNA decay. Others may find the dataset useful.
• This study might complement and/or be informed by another recent study in BioRXiv - https://doi.org/10.1101/2023.09.04.556219
• My field of expertise is mRNA decay - I am qualified to evaluate the findings within the context of this field. I do not have much experience of LC-MS-MS and therefore cannot evaluate the methods/analysis of this part of the study.

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Reply to the reviewers

Revision Plan

Manuscript number: RC-2024-02385

Corresponding author(s): Jennifer R. Kowalski

1. General Statements [optional]

Our manuscript describes a novel role for the conserved glycoprotein hormone receptor, FSHR-1, in regulating C. elegans neuromuscular function through an inter-tissue, gut-brain signaling pathway. FSHR-1 is the sole C. elegans homolog of a family of vertebrate glycoprotein receptors that includes FSHR, TSHR, and LHR, and has previously been shown to regulate body size, germline differentiation, lipid homeostasis, and various stress responses in the worm (Kenis at al 2023; Cho et al 2007; Torzone et al 2023; Powell et al 2009; Miller et al 2015; Robinson and Powell 2016; Wei and Kowalski, 2018; Kim and Sieburth 2020; Wang et al 2023) but its role in neuromuscular regulation, although identified in a 2005 RNA interference screen (Sieburth et al 2005), has not been previously explored. Here, through a combination of genetic, behavioral, and fluorescence imaging approaches, we demonstrate that FSHR-1 is both necessary and sufficient in the intestine of the worm (and may also act in several other distal tissues, including glia and head neurons) to promote muscle excitation through effects on active zone protein localization and synaptic vesicle release from cholinergic motor neurons. Additionally, we identify the FSHR-1 ligands, glycoproteins GPLA-1 and GPLB-1, as well as several known downstream effectors of FSHR-1 in other contexts, GSA-1/GalphaS, ACY-1/adenylyl cyclase, and the lipid kinase SPHK-1, as interactors in the FSHR-1 pathway for neuromuscular control. This work represents a detailed description of the ability of this conserved and multi-functional receptor in inter-tissue coordination that may ultimately be connected to its functions in other physiological processes, such as the stress response, and may also prove relevant for understanding roles for FSHR-1 homologs in humans.

We greatly appreciate the thoughtful and constructive feedback provided by each of the three reviewers of this manuscript. We are pleased that all three reviewers noted the novelty of the mechanisms of cross-tissue regulation of neuromuscular function by FSHR-1 that we uncovered. Reviewer 1 comments, "They demonstrate a novel phenomenon of cross-tissue regulation by restoring FSHR-1 in neurons, intestines, or glia to restore NMJ function." Reviewer 2 echoes this sentiment, also noting, "The data is well presented, compelling and the conclusions are well supported by the data. . .. [T]his study provides a solid foundation to address many interesting questions regarding the role of fshr-1 signaling in regulating neuronal function." Reviewer 3 adds "This is a highly worthy contribution to the field of cell non-autonomous signaling and neuromodulation, and specifically synaptic transmission modulation. The study deepens and enhances the understanding of fshr-1 function within the C. elegans intestine and adds in several molecular components into the signaling pathway, acting both upstream and downstream. . . While this work relies on an invertebrate system of C. elegans, all components have vertebrate counterparts, so findings are likely of broader interest."

As described below, we are working to address many of the comments made by the reviewers and have already made some of the suggested minor changes to the manuscript. We are hopeful that, given the reviewers' excitement about this work, the changes we have already made, and the additional revisions we intend to make in the coming months, including the completion of several new experiments we propose in the revision plan below, our manuscript will be of interest to a broad genetics audience.

2. Description of the planned revisions

Planned Revisions based on comments from Reviewer #1

• __The authors found that expressing FSHR-1 in intestinal cells was sufficient to compensate for the fshr-1 mutation phenotype, suggesting that intestinal cell FSHR-1 can regulate neuromuscular junction (NMJ) function across tissues. However, the molecular mechanism remains unexplored. Since the downstream signaling pathways of FSHR-1 are clear, analyzing the gain-of-function (gf) mutations of gsa-1 and acy-1 in different tissues can help elucidate the signaling pathways transmitted across tissues. __ We completely agree that tissue-specific pathway analysis is important for understanding the molecular mechanism underlying the ability of FSHR-1 to control neuromuscular function from its location in distal tissues, like the intestine. Because of the complexity of these questions and the time required for us to generate strains to perform tissue-specific protein depletion or overexpression experiments, we intend these studies to be the focus of a future manuscript However, in lieu of performing a full suite of tissue-specific analyses of FSHR-1 downstream components, we will perform intestine-specific RNA interference experiments (as we did for fshr-1 in Figure 4B) of gsa-1, acy-1, and sphk-1 in wild type worms and in animals overexpressing fshr-1 in the intestine (which causes increased swimming behavior, Figure 3A) to determine if these downstream players are required for the effects of intestinal fshr-1 on the NMJ. __ __We appreciate the reviewer's suggestion to address these important questions regarding the site of action of the downstream players.

• The images of neurons should be presented in higher resolution and magnification to provide clearer visualization. __ We appreciate the reviewer's request for increased visualization of the neurons; however, because the current larger, lower resolution images show several release sites and were used for the quantitative analyses we present, we would like to keep the images as they are. __However, *we will provide higher resolution insets for the images in Figures 2A, 2C-F, and 4C, as requested. *

• It is unclear whether the glycoprotein subunit orthologs act in the intestine to regulate NMJ function with FSHR-1. This should be investigated and clarified in the manuscript. __ We fully agree that determining where and how the glycoproteins GPLA-1 and GPLB-1 interact with FSHR-1 - and if this is happening at the level of the intestine - is an important outstanding question. Based on prior work, it is known that these subunits are not expressed in intestinal cells, but they are found in several gut-associated neurons and tissues. Specifically, gpla-1 is expressed in neurons of the gastrointestinal tract, including M1, M5, I5 and NSM pharyngeal motor neurons, as well the AVL and DVB excitatory motor neurons that control defecation contractions in the hindgut. gplb-1 is also expressed in the DVB neuron, as well as in non-neuronal tissues (head mesodermal cells and the hindgut enteric muscles), and both glycoprotein genes show reporter expression in the RME motor neurons in the head (Kenis et al 2023). We will complete experiments testing whether the effects of intestinal FSHR-1 overexpression require the ligands, as suggested by Reviewer #2. __We intend that our future work will explore the glycoprotein-FSHR-1 interactions more deeply in a variety of contexts.

• __In Figure 4C, there are no error bars, and individual values should be shown in all statistical analyses to provide a complete representation of the data and its variability. __ We again thank the reviewer for catching this error in Figure 4C. We have replaced the graph with the complete one that includes error bars. We will replace the graphs in 1B, 1C, 3D, 4A, 4C, 5A, 5B, and 6E, as well as Supplemental Figure 5A, 5B, 6A, 6B, 7A, and 7C with bars overlaid with the individual data points. We are unable to do this for Figures 2A-F or Supplemental Figures 2A-C, 7B or 7D because these analyses were run using Custom-written Igor software (Burbea et al 2002) that does not provide individual values, only mean values and cumulative probability plots of the datasets. We recently showed consistency between the Igor analysis program and the newer Fiji plug-in we used for our more recent imaging data, supporting concordance of results despite not having the individual data points in Igor (Hulsey-Vincent et al 2023).

Planned Revisions based on comments from Reviewer #2

• __Fig 4B: An intestinal site of action seems likely for fshr-1 and is nicely supported by the intestine-specific RNAi experiment in Fig 4B. Does intestine-specific knockdown of fshr-1 also cause the aldicarb and SNB-1 defects seen in the mutant? Including this data especially for the synaptic markers would strengthen the gut to neuron inter-tissue signaling model that is proposed here (OPTIONAL). __ We appreciate the reviewer's suggestion to include additional intestine-specific knockdown data for the aldicarb, SNB-1::GFP, and other imaging data. We have the reagents to perform the intestine-specific knockdown of fshr-1 in the aldicarb assay and will complete these experiments as part of our revision plan. Although performing the same experiments in the imaging strains requires first crossing each imaging line to the intestine-specific RNAi line, which may may prove challenging, we are currently working to cross the intestinal RNAi line with nuIs152, the cholinergic SNB-1::GFP line and, assuming the cross goes well, will include results in our revised manuscript.

• Fig 5A: The authors show that G alpha s and adenylyl cyclase function downstream of fshr-1, but it is unclear whether these are direct fshr-1 effectors or whether they function less directly. Does expressing gsa-1(gf) or acy-1(gf) transgenes specifically in the intestine (or neurons) suppress the fshr-1 defects? (OPTIONAL) __ As stated in our response to Reviewer #1, we completely agree that tissue-specific pathway analysis is important for understanding the molecular mechanism underlying the ability of FSHR-1 to control neuromuscular function from its location in distal tissues, like the intestine. While the complexity of these questions and the time required for us to generate strains to perform tissue-specific protein depletion or overexpression experiments is likely more than is suitable for the revision time frame of this manuscript (and will be the focus of future work), in lieu of these experiments we will perform intestine-specific RNA interference experiments (as we did for fshr-1 in Figure 4B) of gsa-1, acy-1, and sphk-1 in wild type worms and in animals overexpressing fshr-1 in the intestine (which causes increased swimming behavior, Figure 3A) to determine if these downstream players are required for the effects of intestinal fshr-1 on the NMJ. __We appreciate the reviewer's suggestion to address these important questions regarding the site of action of the downstream players.

• __Fig 6A-D: The authors propose that fshr-1 is activated by its ligands for locomotion, but no evidence is presented to support this. This could be experimentally addressed with the reagents that are used in this study by determining whether the increased locomotion caused by overexpressing fshr-1 in the intestine (reported in Fig 3A), is dependent upon gpla-1 and/or gplb-1 activity. This experiment would help to distinguish whether gpla-1 and/or gplb-1 indeed are fshr-1 ligands or whether fshr-1 functions in a ligand-independent manner, and would justify the sentence on line 526 "...ligands...act upstream in this context..." __ We agree with the reviewer that the question of GP ligand activation of FSHR-1 in this context is an important and interesting question. We plan to cross the intestinal fshr-1 transgene into the gpla-1, gplb-1, and gpla-1gplb-1 mutants, as suggested and then will test their swimming behavior to see if the overexpression effect depends upon the ligands. We thank the reviewer for this experimental suggestion.

Planned Revisions based on comments from Reviewer #3

• __Within Figure 6, the authors state that an experiment was run 2-3X which seems inconsistent with other figure panels. It would be better if three times was consistently used. Adding in another run seems appropriate. To add another experimental run where needed within Figure 6 A-D seems realistic. The strains, reagents and skills are all in place, so the only significant investment is time. These experiments should be able to be completed in a few weeks/months. __ We appreciate the reviewer's desire for consistency in terms of the number of replicates. We will ensure all swimming experiments, which were the experiments in question in Figure 6, have been completed at least 3 times as part of our revision plan.

• The authors findings would be strengthened by doing further work to delineate in which tissues the downstream factors act, by doing tissue specific epistasis basically for gsa-1, acy-1 etc. This would entail a lot of work and would delay publication significantly. I do not see this as necessary unless the authors wish for a big impact journal publication. __ As stated in our response to Reviewers #1 and 2, we agree that tissue-specific pathway analysis is important for understanding the molecular mechanism underlying the ability of FSHR-1 to control neuromuscular function from its location in distal tissues, like the intestine. While the complexity of these questions and the time required for us to generate strains to perform tissue-specific protein depletion or overexpression experiments is likely more than is suitable for the revision time frame of this manuscript (and will be the focus of future work), in lieu of these experiments we will perform intestine-specific RNA interference experiments (as we did for fshr-1 in Figure 4B) of gsa-1, acy-1, and sphk-1 in wild type worms and in animals overexpressing fshr-1 in the intestine (which causes increased swimming behavior, Figure 3A) to determine if these downstream players are required for the effects of intestinal fshr-1 on the NMJ. __We appreciate the reviewer's suggestion to address these important questions regarding the site of action of the downstream players.

• __Figures:____ Overall the authors have presented everything in a clear and thorough manner. Some modification of the Y-axes on several aldicarb resistance graphs & body bend bar graphs could improve the clarity. Trying to standardize the Y axis range and the tick mark locations would make it easier to read and compare between figures and panels. __ We appreciate the reviewer's attention to detail here and will work to further standardize the Y-axes on the graphs as requested.

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

Revisions made to the manuscript in response to comments by Reviewer #1

• __The authors should demonstrate the expression of FSHR-1 in various tissues, as this is essential for analyzing its function. __ We appreciate the reviewer's request for additional clarity regarding the sites of tissue-specific FSHR-1 expression and agree that this information was not sufficiently clear in the text. It is already known that FSHR-1 is expressed in various tissues (e.g., head neurons, glia, intestine) from prior studies (Cho et al, 2007; Kenis et al 2023; Hammarlund et al 2018); thus, we would like to defer to Reviewer #3's suggestion about the expression information and have added a description of FSHR-1 expression patterns to lines 129 -130 within the Introduction of the paper. (Reviewer #3: "In the discussion there is a section about the reported areas of endogenous fshr-1 expression. I would have appreciated knowing that information much earlier in the paper. Without being reminded of the reported normal expression pattern it is difficult to fully appreciate why how the neuronal and glial expression could be at work") This expression information is also mentioned in the Results section lines 420-421 when we first discuss the tissue-specific rescue experiments.

• __Figure 4A appears to be the same as Figure S5B. The authors should ensure that the figures are correctly labeled and distinct from each other. __ We thank the reviewer for noticing this oversight. We apologize for the inadvertent duplication. We have replaced the graphs in Figure 4A with the correct rescue experiment using the Pges-1, ibtEx35-expressing strain.

Revisions made to the manuscript in response to comments by Reviewer #2

• Fig 3: Using transgenic rescue experiments the authors observe rescue when expressing fshr-1 under promoters for the intestine as well as glia and neurons. Is it possible that the apparent rescue using glia and neuronal promoters may arise from leaky expression of these transgenes in the intestine? Leaky intestinal expression is a reported caveat for rescue experiments. This possibility should be discussed. We appreciate the reviewer's note regarding the potential caveat of leaky intestinal expression. We have added a mention of this possibility to the discussion (lines 612-616) where we outline other potential explanations for the ability of multiple transgenes to rescue the neuromuscular phenotype. This possibility is why we feel most confident in the intestine site of action given that we have intestine-specific RNA interference data showing fshr-1 necessity in this tissue. We also acknowledge the need for tissue-specific depletion studies to address requirements for fshr-1 in the other distal tissues. We hope to be able to address these other potential sites of action in our future work.

• __Fig 4B: Please clarify at what stage the intestine-specific knockdown of fshr-1 was conducted. It would be informative to treat animals with fshr-1 RNAi at various developmental stages to distinguish whether fshr-1 plays a developmental or post-developmental role in this process (OPTIONAL). __ We thank the reviewer for bringing to our attention the omission of details regarding the feeding RNA interference experiments. We have added an "RNA Interference" subsection with this information to the Materials and Methods section of the manuscript. Briefly, the intestine-specific knockdown was performed by feeding worms at the L4 stage HT115(DE) bacteria containing L4440 empty plasmid or one targeting fshr-1. Worms were grown for 4 days on NGM agar plates containing Ampicillin and IPTG, then offspring of the treated worms were assayed at the young adult stage. Thus, the knockdown animals we tested had been exposed to the RNAi for their lifetime. We are very interested in exploring the developmental timing of fshr-1 expression and function in future work; thus, we thank the reviewer for this suggestion. However, we feel that a detailed panel of developmental knockdown effects of fshr-1 is beyond the scope of the current study.

• Fig 4C: Is rescue significant? p values are not shown. In figure 4C, p-values are only shown for statistically significant differences, as noted in the figure legend. A Tukey's post-hoc test indicates that the Intestinal Rescue strain is not significantly different from either the wild type or the fshr-1 mutants, indicating partial rescue. While we cannot fully explain the discrepancy between the partial rescue of the SNB-1::GFP phenotype in light of the full behavioral rescue in the swimming, aldicarb, and crawling assays, we suspect it may be due to the fact that synaptic vesicle release has been sufficiently restored to recover neuromuscular signaling even though synaptic vesicle localization is not fully returned to wild type levels, given the variable and likely non-endogenous levels of fshr-1 re-expression from the tissue-specific transgenes. We have noted this discrepancy in the Discussion (lines 633-639) when considering the levamisole and SNB-1::GFP data in light of the aldicarb and swimming results. * "*For some tissue-specific fshr-1 expression experiments, we observed partial rescue of the swimming and crawling fshr-1 mutant phenotypes without a restoration of normal synaptic vesicle localization (e.g., cholinergic motor neurons, GABAergic motor neurons, glial cells, Supplemental Figures 6 and 7). We conclude that GFP::SNB-1 accumulation may not solely report on rates of synaptic vesicle release and/or that there are compensatory mechanisms for increasing muscle excitation (e.g. upregulation of postsynaptic ACh receptors or muscle excitatory machinery."

• __Fig 6E. There are two bars in this graph labeled gpla-1; gplb-1 that show significantly different amplitudes. Please clarify and define the different colors that each graph is outlined with. __ We thank the reviewer for catching this error. The third bar from the left should say "gpla-1;fshr-1". We have corrected this in the manuscript. We have also added descriptions of the colors to the figure legend indicating the following: dark blue = wild type, yellow = fshr-1; green = glycopeptide mutants; blue = glycopeptide;fshr-1 mutants. Similar clarification has been added to the legend for the bar graph in Figure 3D.

Revisions made to the manuscript in response to comments by Reviewer #3

Suggested Text Revisions: I have some suggestions to consider.

• In the abstract the term expression analysis is used to analyses of areas of FSHR-1 function using tissue specific rescue experiments. Expression analysis often means directly exploring mRNA, localization, or levels using transcriptomic approaches or reporter genes so some revision of language could improve accuracy in the abstract. We appreciate the reviewer's point and have removed the phrase "expression analysis" from the summary at the end of the Introduction section where it initially appeared.

• __In Figure 1, the authors do not comment on the overexpression phenotype or why this strain was included. __ We thank the reviewer for noticing this oversight. We have added a sentence describing the overexpression experiment and its implications in our description of Figure 1 in the Results section (lines 337-339).

• __In the discussion there is a section about the reported areas of endogenous fshr-1 expression. I would have appreciated knowing that information much earlier in the paper. Without being reminded of the reported normal expression pattern it is difficult to fully appreciate why how the neuronal and glial expression could be at work. __ We appreciate the reviewer's request for additional clarity regarding the sites of tissue-specific FSHR-1 expression and agree that this information was not sufficiently clear in the text prior to the discussion. We have added a description of FSHR-1 expression patterns to lines 129 -130 within the Introduction of the paper. It is also mentioned in Results section lines 420-421 when we first discuss the tissue-specific rescue experiments.

• __The section on tissue specific rescue could be written more strongly. The use of many "transition" phrases dilutes the importance of the findings in this paragraph. __ We are grateful for the reviewer's suggestions to improve the clarity of the text, specifically regarding the tissue-specific rescue section. We have tightened up the text in this section of the Discussion (lines 547-621) to remove some of the transitional phrases. We believe this has enhanced the readability of the manuscript and the impact of our findings.

• Figures: __ 3 panel D: it is not clear what the last 2 bars (Neuronal rescues) are being compared to, its it w.t.? Were the differences between fshr-1 and these rescues not significantly different? __ We appreciate the reviewer bringing this point of confusion to our attention with Figure 3D. We have clarified in the figure legend that the Neuronal rescue bars are compared to wild type and that there is no significant difference from the fshr-1 mutants for these two lines, further supporting our central focus on the intestine as the best-supported site of FSHR-1 action.

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

Comment from Reviewer #1

• __The article concludes that the fshr-1 mutation affects the release of acetylcholine vesicles. However, using fluorescent proteins to label key proteins released by vesicles may introduce artifacts. Therefore, electron microscopy should be used to analyze vesicle accumulation for more reliable results. __ We thank the reviewers for this suggestion and acknowledge the potential value of EM to definitively show vesicle accumulation in fshr-1 mutants. However, these experiments are technically demanding, involve specialized high-pressure freezing, and would require us to establish new collaborations to complete; thus, we would not be able to be complete such experiments in a timeframe reasonable for revision. While the fluorescence microscopy experiments admittedly offer less resolution, this approach has been used with great success in numerous other studies to identify alterations in synaptic vesicle localization in motor neurons that correlate with electron microscopy, electrophysiology, and aldicarb data that more directly measure numbers of synaptic vesicles and synaptic function (Jorgensen et al 1995; Jin et al 1999; Nonet et al 1999). Thus, we believe that the pHluorin experiments, coupled with the SNB-1::GFP imaging, are sufficient to demonstrate defects in vesicle release, regardless of the specific effects on vesicle clustering. We have been mindful not to overstate our conclusions (lines 371-372: "Together, these data demonstrate that FSHR-1 signaling promotes the localization and/or release of cholinergic synaptic vesicles.") We hope the reviewer will agree that our analysis provides meaningful information about SV organization in the absence of EM level experiments.

• __The authors analyzed the release of vesicles from GABA and acetylcholine (Ach) neurons separately to demonstrate that the fshr-1 mutation specifically affects Ach neuron vesicle release. However, while GFP::SNB-1 and GFP::SYD-1 accumulated in GABA neurons, mCherry::UNC-10 did not change significantly in GABA neurons. To fully understand vesicle release, the authors should also use synaptopHluroin (SpH) to analyze GABA neuron vesicle release. __ We agree that our data indicate that, in addition to effects on cholinergic synaptic vesicle release, there may be effects on release of vesicles from GABAergic neurons, and we acknowledge this in the manuscript. However, while we are interested in potentially exploring the effects of fshr-1 in GABAergic neurons, we believe this question requires extensive additional work that is beyond the scope of this manuscript, which is focused on fshr-1 effects on cholinergic signaling. Moreover, given that fshr-1-deficient animas are aldicarb resistant (Figure 1A), it is unlikely that GABA release is decreased. If GABA release was decreased, we would expect hypersensitivity to aldicarb. Thus, while it is still possible there are different effects on GABA vesicles, our data suggest the most physiological relevant effect is on cholinergic signaling. We do acknowledge in the Discussion that it will be of interest to determine the relevance of effects in the GABA neurons (lines 649-651).

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Referee #3

Evidence, reproducibility and clarity

The authors investigate fshr-1's role in regulation of NMJ signaling using a variety of assays within C. elegans. The power of epistatic analyses is employed to fill in the upstream and downstream signaling components of this non-cell autonomous signaling pathway. The study is strengthened by the inclusion of assays that allow multiple levels of functionality to be assessed, including pharmacological sensitivities, vesicle fusion, locomotory traits and synaptic marker protein distributions.

The study shows that fshr-1 acts within the intestine to set off a signaling cascade that alters NMJ function and aspects of synaptic transmission. Intestinal activity is both necessary and sufficient. Expression of fshr-1 in other areas, while not necessarily linked to endogenous expression, can rescue many NMJ functional activities and some SV localization markers. Ligands for FSHR-1, GPLA-1A and GPLA-1B, were identified using epistasis, as were several downstream signaling components, namely GSA-1, ACY-1 and SPHK-1. The key conclusions are convincing and the authors have stayed truthful and circumspect in their experimental interpretations.

Within Figure 6, the authors state that an experiment was run 2-3X which seems inconsistent with other figure panels. It would be better if three times was consistently used. Adding in another run seems appropriate. To add another experimental run where needed within Figure 6 A-D seems realistic. The strains, reagents and skills are all in place, so the only significant investment is time. These experiments should be able to be completed in a few weeks/months.

The authors findings would be strengthened by doing further work to delineate in which tissues the downstream factors act, by doing tissue specific epistasis basically for gsa-1, acy-1 etc. This would entail a lot of work and would delay publication significantly. I do not see this as necessary unless the authors wish for a big impact journal publication.

Smaller comments for improvement:

Text: I have some suggestions to consider. In the abstract the term expression analysis is used to analyses of areas of FSHR-1 function using tissue specific rescue experiments. Expression analysis often means directly exploring mRNA, localization, or levels using transcriptomic approaches or reporter genes so some revision of language could improve accuracy in the abstract.

In Figure 1, the authors do not comment on the overexpression phenotype or why this strain was included.

In the discussion there is a section about the reported areas of endogenous fshr-1 expression. I would have appreciated knowing that information much earlier in the paper. Without being reminded of the reported normal expression pattern it is difficult to fully appreciate why how the neuronal and glial expression could be at work.

The section on tissue specific rescue could be written more strongly. The use of many "transition" phrases dilutes the importance of the findings in this paragraph.

Figures: Overall the authors have presented everything in a clear and thorough manner. Some modification of the Y-axes on several aldicarb resistance graphs & body bend bar graphs could improve the clarity. Trying to standardize the Y axis range and the tick mark locations would make it easier to read and compare between figures and panels.

Fig. 3 panel D: it is not clear what the last 2 bars (Neuronal rescues) are being compared to, its it w.t.? Were the differences between fshr-1 and these rescues not significantly different?

Significance

This is a highly worthy contribution to the field of cell non-autonomous signaling and neuromodulation, and specifically synaptic transmission modulation. The study deepens and enhances the understanding of fshr-1 function within the C. elegans intestine and adds in several molecular components into the signaling pathway, acting both upstream and downstream. The authors were able to define the output of intestinal fshr-1 function in relation to synaptic vesicle localization and fusion using the pHlourin assay which significantly extends our understanding of the mechanistic dissection of the non-autonomous regulation of Ach synaptic transmission. The manuscript is written with care and insight. The discussion contextualizes the study's findings in relation to the prior studies with care and attempts to elucidate how their findings interrelate.

This would be of high interest to those focused on neuromodulation, synaptic function, and signaling. While this work relies on an invertebrate system of C. elegans, all components have vertebrate counterparts, so findings are likely of broader interest.

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Referee #2

Evidence, reproducibility and clarity

In this study Buckley et al. examine the role of the follicle stimulating hormone receptor homolog FSHR-1 in regulating excitatory neurotransmission at worm neuromuscular junctions (NMJs). They showed that mutations in fshr-1 impair neuromuscular function as measured by aldicarb sensitivity, movement, and abundance of presynaptic markers. They show that these defects can be rescued by expressing fshr-1 in the intestine, glia and neurons to varying extents. Using genetic epistasis analysis, they identify two potential FSHR-1 effectors that function downstream of fshr-1 to control locomotion. Finally, they show that mutations in genes that share homology to mammalian FSH ligands function in a common genetic pathway with fshr-1 to promote locomotion. The authors propose that fshr-1 is part of an inter tissue signaling pathway by which tissues such as the intestine can regulate cholinergic function. The authors have presented a clear story by utilizing genetics, behavioral analysis, and synaptic imaging to demonstrate that intestinal fshr-1 positively regulates cholinergic signaling. The data is well presented, compelling and the conclusions are well supported by the data. The study reinforces prior studies that implicate fshr-1 in positively regulating cholinergic signaling, and the authors use largely indirect assays (movement) to evaluate NMJ function, limiting conceptual and mechanistic advances. However, this study provides a solid foundation to address many interesting questions regarding the role of fshr-1 signaling in regulating neuronal function.

Comments:

1. Fig 3: Using transgenic rescue experiments the authors observe rescue when expressing fshr-1 under promoters for the intestine as well as glia and neurons. Is it possible that the apparent rescue using glia and neuronal promoters may arise from leaky expression of these transgenes in the intestine? Leaky intestinal expression is a reported caveat for rescue experiments. This possibility should be discussed.
2. Fig 4B: An intestinal site of action seems likely for fshr-1, and is nicely supported by the intestine-specific RNAi experiment in Fig 4B. Does intestine-specific knockdown of fshr-1 also cause the aldicarb and SNB-1 defects seen in the mutant? Including this data especially for the synaptic markers would strengthen the gut to neuron inter-tissue signaling model that is proposed here (OPTIONAL).
3. Fig 4B: Please clarify at what stage the intestine-specific knockdown of fshr-1 was conducted. It would be informative to treat animals with fshr-1 RNAi at various developmental stages to distinguish whether fshr-1 plays a developmental or post-developmental role in this process (OPTIONAL).
4. Fig 5A: The authors show that G alpha s and adenylyl cyclase function downstream of fshr-1, but it is unclear whether these are direct fshr-1 effectors or whether they function less directly. Does expressing gsa-1(gf) or acy-1(gf) transgenes specifically in the intestine (or neurons) suppress the fshr-1 defects? (OPTIONAL)
5. Fig 6A-D: The authors propose that fshr-1 is activated by its ligands for locomotion, but no evidence is presented to support this. This could be experimentally addressed with the reagents that are used in this study by determining whether the increased locomotion caused by overexpressing fshr-1 in the intestine (reported in Fig 3A), is dependent upon gpla-1 and/or gplb-1 activity. This experiment would help to distinguish whether gpla-1 and/or gplb-1 indeed are fshr-1 ligands or whether fshr-1 functions in a ligand-independent manner, and would justify the sentence on line 526 "...ligands...act upstream in this context..."
6. Fig 4C: Is rescue significant? p values are not shown.
7. Fig 6E. There are two bars in this graph labeled gpla-1; gplb-1 that show significantly different amplitudes. Please clarify and define the different colors that each graph is outlined with.

Significance

The authors have presented a clear story by utilizing genetics, behavioral analysis, and synaptic imaging to demonstrate that intestinal fshr-1 positively regulates cholinergic signaling. The data is well presented, compelling and the conclusions are well supported by the data. The study reinforces prior studies that implicate fshr-1 in positively regulating cholinergic signaling, and the authors use largely indirect assays (movement) to evaluate NMJ function, limiting conceptual and mechanistic advances. However, this study provides a solid foundation to address many interesting questions using a powerful genetic model organism regarding the role of fshr-1 signaling in regulating neuronal function.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, the authors investigate the role of the glycoprotein hormone receptor FSHR-1 in regulating cholinergic neurotransmission. They first demonstrate that fshr-1 mutants exhibit strong resistance to the acetylcholine esterase inhibitor aldicarb, consistent with previous findings (Sieburth et al., 2005). The authors further analyze other behaviors of the fshr-1 mutant and conclude that the fshr-1 gene affects neuromuscular regulation.

Next, the authors use GFP::SNB-1 to label acetylcholine neuron vesicles and observe a significant accumulation of GFP::SNB-1 in neurons of the fshr-1 mutant. Using fluorescence recovery after photobleaching (FRAP) experiments with synaptopHluroin (SpH) to label vesicle release, they find a reduction in vesicle release in the fshr-1 mutant.

Furthermore, the authors re-express fshr-1 in the intestine, glia, or neurons of fshr-1 mutants and find that this restoration restores neuromuscular function. They focus on intestinal fshr-1 re-expression for further study, showing that it partially restores the aberrant synaptic vesicle accumulation seen in fshr-1 mutants. Lastly, the authors investigate the involvement of GPLA-1 and GPLB-1, the ligands of FSHR-1, and GSA-1, ACY-1, and SPHK-1, downstream factors of FSHR-1, in the same signaling pathway as fshr-1 in regulating neuromuscular function.

In summary, the authors explore the phenotypes of aldicarb resistance in fshr-1 mutants and confirm the reduction of acetylcholine release in the fshr-1 mutant by labeling the process of acetylcholine neuronal vesicle release. They also analyze the involvement of FSHR-1 ligands and downstream factors in its regulation of the neuromuscular junction (NMJ). Furthermore, they demonstrate a novel phenomenon of cross-tissue regulation by restoring FSHR-1 in neurons, intestines, or glia to restore NMJ function. However, the underlying mechanisms of this cross-tissue regulation remain unexplored.

Major point:

1. The article concludes that the fshr-1 mutation affects the release of acetylcholine vesicles. However, using fluorescent proteins to label key proteins released by vesicles may introduce artifacts. Therefore, electron microscopy should be used to analyze vesicle accumulation for more reliable results.
2. The authors analyzed the release of vesicles from GABA and acetylcholine (Ach) neurons separately to demonstrate that the fshr-1 mutation specifically affects Ach neuron vesicle release. However, while GFP::SNB-1 and GFP::SYD-1 accumulated in GABA neurons, mCherry::UNC-10 did not change significantly in GABA neurons. To fully understand vesicle release, the authors should also use synaptopHluroin (SpH) to analyze GABA neuron vesicle release.
3. The authors found that expressing FSHR-1 in intestinal cells was sufficient to compensate for the fshr-1 mutation phenotype, suggesting that intestinal cell FSHR-1 can regulate neuromuscular junction (NMJ) function across tissues. However, the molecular mechanism remains unexplored. Since the downstream signaling pathways of FSHR-1 are clear, analyzing the gain-of-function (gf) mutations of gsa-1 and acy-1 in different tissues can help elucidate the signaling pathways transmitted across tissues.
4. The images of neurons should be presented in higher resolution and magnification to provide clearer visualization.

Minor point:

1. The authors should demonstrate the expression of FSHR-1 in various tissues, as this is essential for analyzing its function.
2. It is unclear whether the glycoprotein subunit orthologs act in the intestine to regulate NMJ function with FSHR-1. This should be investigated and clarified in the manuscript.
3. Figure 4A appears to be the same as Figure S5B. The authors should ensure that the figures are correctly labeled and distinct from each other.
4. In Figure 4C, there are no error bars, and individual values should be shown in all statistical analyses to provide a complete representation of the data and its variability.

Significance

They demonstrate a novel phenomenon of cross-tissue regulation by restoring FSHR-1 in neurons, intestines, or glia to restore NMJ function.

However, the underlying mechanisms of this cross-tissue regulation remain unexplored.

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Reply to the reviewers

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

I have trialled the package on my lab's data and it works as advertised. It was straightforward to use and did not require any special training. I am confident this is a tool that will be approachable even to users with limited computational experience. The use of artificial data to validate the approach - and to provide clear limits on applicability - is particularly helpful.

The main limitation of the tool is that it requires the user to manually select regions. This somewhat limits the generalisability and is also more subjective - users can easily choose "nice" regions that better match with their hypothesis, rather than quantifying the data in an unbiased manner. However, given the inherent challenges in quantifying biological data, such problems are not easily circumventable.

*

* I have some comments to clarify the manuscript:

1. A "straightforward installation" is mentioned. Given this is a Method paper, the means of installation should be clearly laid out.*

__This sentence is now modified. In the revised manuscript we now describe how to install the toolset and we give the link to the toolset website if further information is needed. __On this website, we provide a full video tutorial and a user manual. The user manual is provided as a supplementary material of the manuscript.

* It would be helpful if there was an option to generate an output with the regions analysed (i.e., a JPG image with the data and the drawn line(s) on top). There are two reasons for this: i) A major problem with user-driven quantification is accidental double counting of regions (e.g., a user quantifies a part of an image and then later quantifies the same region). ii) Allows other users to independently verify measurements at a later time.*

We agree that it is helpful to save the analyzed regions. To answer this comment and the other two reviewers' comments pointing at a similar feature, we have now included an automatic saving of the regions of interest. The user will be able to reopen saved regions of interest using a new function we included in the new version of PatternJ.

* 3. Related to the above point, it is highlighted that each time point would need to be analysed separately (line 361-362). It seems like it should be relatively straightforward to allow a function where the analysis line can be mapped onto the next time point. The user could then adjust slightly for changes in position, but still be starting from near the previous timepoint. Given how prevalent timelapse imaging is, this seems like (or something similar) a clear benefit to add to the software.*

We agree that the analysis of time series images can be a useful addition. We have added the analysis of time-lapse series in the new version of PatternJ. The principles behind the analysis of time-lapse series and an example of such analysis are provided in Figure 1 - figure supplement 3 and Figure 5, with accompanying text lines 140-153 and 360-372. The analysis includes a semi-automated selection of regions of interest, which will make the analysis of such sequences more straightforward than having to draw a selection on each image of the series. The user is required to draw at least two regions of interest in two different frames, and the algorithm will automatically generate regions of interest in frames in which selections were not drawn. The algorithm generates the analysis immediately after selections are drawn by the user, which includes the tracking of the reference channel.

* Line 134-135. The level of accuracy of the searching should be clarified here. This is discussed later in the manuscript, but it would be helpful to give readers an idea at this point what level of tolerance the software has to noise and aperiodicity.

*

We agree with the reviewer that a clarification of this part of the algorithm will help the user better understand the manuscript.__ We have modified the sentence to clarify the range of search used and the resulting limits in aperiodicity (now lines 176-181). __Regarding the tolerance to noise, it is difficult to estimate it a priori from the choice made at the algorithm stage, so we prefer to leave it to the validation part of the manuscript. We hope this solution satisfies the reviewer and future users.

*

**Referees cross-commenting**

I think the other reviewer comments are very pertinent. The authors have a fair bit to do, but they are reasonable requests. So, they should be encouraged to do the revisions fully so that the final software tool is as useful as possible.

Reviewer #1 (Significance (Required)):

Developing software tools for quantifying biological data that are approachable for a wide range of users remains a longstanding challenge. This challenge is due to: (1) the inherent problem of variability in biological systems; (2) the complexity of defining clearly quantifiable measurables; and (3) the broad spread of computational skills amongst likely users of such software.

In this work, Blin et al., develop a simple plugin for ImageJ designed to quickly and easily quantify regular repeating units within biological systems - e.g., muscle fibre structure. They clearly and fairly discuss existing tools, with their pros and cons. The motivation for PatternJ is properly justified (which is sadly not always the case with such software tools).

Overall, the paper is well written and accessible. The tool has limitations but it is clearly useful and easy to use. Therefore, this work is publishable with only minor corrections.

*We thank the reviewer for the positive evaluation of PatternJ and for pointing out its accessibility to the users.

*

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

# Summary

The authors present an ImageJ Macro GUI tool set for the quantification of one-dimensional repeated patterns that are commonly occurring in microscopy images of muscles.

# Major comments

In our view the article and also software could be improved in terms of defining the scope of its applicability and user-ship. In many parts the article and software suggest that general biological patterns can be analysed, but then in other parts very specific muscle actin wordings are used. We are pointing this out in the "Minor comments" sections below. We feel that the authors could improve their work by making a clear choice here. One option would be to clearly limit the scope of the tool to the analysis of actin structures in muscles. In this case we would recommend to also rename the tool, e.g. MusclePatternJ. The other option would be to make the tool about the generic analysis of one-dimensional patterns, maybe calling the tool LinePatternJ. In the latter case we would recommend to remove all actin specific wordings from the macro tool set and also the article should be in parts slightly re-written.

*

We agree with the reviewer that our initial manuscript used a mix of general and muscle-oriented vocabulary, which could make the use of PatternJ confusing especially outside of the muscle field. To make PatternJ useful for the largest community, we corrected the manuscript and the PatternJ toolset to provide the general vocabulary needed to make it understandable for every biologist. We modified the manuscript accordingly.

* # Minor/detailed comments

# Software

We recommend considering the following suggestions for improving the software.

## File and folder selection dialogs

In general, clicking on many of the buttons just opens up a file-browser dialog without any further information. For novel users it is not clear what the tool expects one to select here. It would be very good if the software could be rewritten such that there are always clear instructions displayed about which file or folder one should open for the different buttons.*

We experienced with the current version of macOS that the file-browser dialog does not display any message; we suspect this is the issue raised by the reviewer. This is a known issue of Fiji on Mac and all applications on Mac since 2016. We provided guidelines in the user manual and on the tutorial video to correct this issue by changing a parameter in Fiji. Given the issues the reviewer had accessing the material on the PatternJ website, which we apologize for, we understand the issue raised. We added an extra warning on the PatternJ website to point at this problem and its solution. Additionally, we have limited the file-browser dialog appearance to what we thought was strictly necessary. Thus, the user will experience fewer prompts, speeding up the analysis.

*

## Extract button

The tool asks one to specify things like whether selections are drawn "M-line-to-M-line"; for users that are not experts in muscle morphology this is not understandable. It would be great to find more generally applicable formulations. *

We agree that this muscle-oriented vocabulary can make the use of PatternJ confusing. We have now corrected the user interface to provide both general and muscle-specific vocabulary ("center-to-center or edge-to-edge (M-line-to-M-line or Z-disc-to-Z-disc)").*

## Manual selection accuracy

The 1st step of the analysis is always to start from a user hand-drawn profile across intensity patterns in the image. However, this step can cause inaccuracy that varies with the shape and curve of the line profile drawn. If not strictly perpendicular to for example the M line patterns, the distance between intensity peaks will be different. This will be more problematic when dealing with non-straight and parallelly poised features in the image. If the structure is bended with a curve, the line drawn over it also needs to reproduce this curve, to precisely capture the intensity pattern. I found this limits the reproducibility and easy-usability of the software.*

We understand the concern of the reviewer. On curved selections this will be an issue that is difficult to solve, especially on "S" curved or more complex selections. The user will have to be very careful in these situations. On non-curved samples, the issue may be concerning at first sight, but the errors go with the inverse of cosine and are therefore rather low. For example, if the user creates a selection off by 5 degrees, which is visually obvious, lengths will be affected by an increase of only 0.38%. The point raised by the reviewer is important to discuss, and we therefore added a paragraph to comment on the choice of selection (lines 94-98) and a supplementary figure to help make it clear (Figure 1 - figure supplement 1).*

### Reproducibility

Since the line profile drawn on the image is the first step and very essential to the entire process, it should be considered to save together with the analysis result. For example, as ImageJ ROI or ROIset files that can be re-imported, correctly positioned, and visualized in the measured images. This would greatly improve the reproducibility of the proposed workflow. In the manuscript, only the extracted features are being saved (because the save button is also just asking for a folder containing images, so I cannot verify its functionality). *

We agree that this is a very useful and important feature. We have added ROI automatic saving. Additionally, we now provide a simplified import function of all ROIs generated with PatternJ and the automated extraction and analysis of the list of ROIs. This can be done from ROIs generated previously in PatternJ or with ROIs generated from other ImageJ/Fiji algorithms. These new features are described in the manuscript in lines 120-121 and 130-132.

*

## ? button

It would be great if that button would open up some usage instructions.

*

We agree with the reviewer that the "?" button can be used in a better way. We have replaced this button with a Help menu, including a simple tutorial showing a series of images detailing the steps to follow by the user, a link to the user website, and a link to our video tutorial.

* ## Easy improvement of workflow

I would suggest a reasonable expansion of the current workflow, by fitting and displaying 2D lines to the band or line structure in the image, that form the "patterns" the author aims to address. Thus, it extracts geometry models from the image, and the inter-line distance, and even the curve formed by these sets of lines can be further analyzed and studied. These fitted 2D lines can be also well integrated into ImageJ as Line ROI, and thus be saved, imported back, and checked or being further modified. I think this can largely increase the usefulness and reproducibility of the software.

*

We hope that we understood this comment correctly. We had sent a clarification request to the editor, but unfortunately did not receive an answer within the requested 4 weeks of this revision. We understood the following: instead of using our 1D approach, in which we extract positions from a profile, the reviewer suggests extracting the positions of features not as a single point, but as a series of coordinates defining its shape. If this is the case, this is a major modification of the tool that is beyond the scope of PatternJ. We believe that keeping our tool simple, makes it robust. This is the major strength of PatternJ. Local fitting will not use line average for instance, which would make the tool less reliable.

* # Manuscript

We recommend considering the following suggestions for improving the manuscript. Abstract: The abstract suggests that general patterns can be quantified, however the actual tool quantifies specific subtypes of one-dimensional patterns. We recommend adapting the abstract accordingly.

*

We modified the abstract to make this point clearer.

* Line 58: Gray-level co-occurrence matrix (GLCM) based feature extraction and analysis approach is not mentioned nor compared. At least there's a relatively recent study on Sarcomeres structure based on GLCM feature extraction: https://github.com/steinjm/SotaTool with publication: *https://doi.org/10.1002/cpz1.462

• *

We thank the reviewer for making us aware of this publication. We cite it now and have added it to our comparison of available approaches.

* Line 75: "...these simple geometrical features will address most quantitative needs..." We feel that this may be an overstatement, e.g. we can imagine that there should be many relevant two-dimensional patterns in biology?!*

We have modified this sentence to avoid potential confusion (lines 76-77).

• *

• Line 83: "After a straightforward installation by the user, ...". We think it would be convenient to add the installation steps at this place into the manuscript. *

__This sentence is now modified. We now mention how to install the toolset and we provide the link to the toolset website, if further information is needed (lines 86-88). __On the website, we provide a full video tutorial and a user manual.

* Line 87: "Multicolor images will give a graph with one profile per color." The 'Multicolor images' here should be more precisely stated as "multi-channel" images. Multi-color images could be confused with RGB images which will be treated as 8-bit gray value (type conversion first) images by profile plot in ImageJ. *

We agree with the reviewer that this could create some confusion. We modified "multicolor" to "multi-channel".

* Line 92: "...such as individual bands, blocks, or sarcomeric actin...". While bands and blocks are generic pattern terms, the biological term "sarcomeric actin" does not seem to fit in this list. Could a more generic wording be found, such as "block with spike"? *

We agree with the reviewer that "sarcomeric actin" alone will not be clear to all readers. We modified the text to "block with a central band, as often observed in the muscle field for sarcomeric actin" (lines 103-104). The toolset was modified accordingly.

* Line 95: "the algorithm defines one pattern by having the features of highest intensity in its centre". Could this be rephrased? We did not understand what that exactly means.*

We agree with the reviewer that this was not clear. We rewrote this paragraph (lines 101-114) and provided a supplementary figure to illustrate these definitions (Figure 1 - figure supplement 2).

* Line 124 - 147: This part the only description of the algorithm behind the feature extraction and analysis, but not clearly stated. Many details are missing or assumed known by the reader. For example, how it achieved sub-pixel resolution results is not clear. One can only assume that by fitting Gaussian to the band, the center position (peak) thus can be calculated from continuous curves other than pixels. *

Note that the two sentences introducing this description are "Automated feature extraction is the core of the tool. The algorithm takes multiple steps to achieve this (Fig. S2):". We were hoping this statement was clear, but the reviewer may refer to something else. We agree that the description of some of the details of the steps was too quick. We have now expanded the description where needed.

* Line 407: We think the availability of both the tool and the code could be improved. For Fiji tools it is common practice to create an Update Site and to make the code available on GitHub. In addition, downloading the example file (https://drive.google.com/file/d/1eMazyQJlisWPwmozvyb8VPVbfAgaH7Hz/view?usp=drive_link) required a Google login and access request, which is not very convenient; in fact, we asked for access but it was denied. It would be important for the download to be easier, e.g. from GitHub or Zenodo.

*

We are sorry for issues encountered when downloading the tool and additional material. We thank the reviewer for pointing out these issues that limited the accessibility of our tool. We simplified the downloading procedure on the website, which does not go through the google drive interface nor requires a google account. Additionally, for the coder community the code, user manual and examples are now available from GitHub at github.com/PierreMangeol/PatternJ, and are provided as supplementary material with the manuscript. To our knowledge, update sites work for plugins but not for macro toolsets. Having experience sharing our codes with non-specialists, a classical website with a tutorial video is more accessible than more coder-oriented websites, which deter many users.

* Reviewer #2 (Significance (Required)):

The strength of this study is that a tool for the analysis of one-dimensional repeated patterns occurring in muscle fibres is made available in the accessible open-source platform ImageJ/Fiji. In the introduction to the article the authors provide an extensive review of comparable existing tools. Their new tool fills a gap in terms of providing an easy-to-use software for users without computational skills that enables the analysis of muscle sarcomere patterns. We feel that if the below mentioned limitations could be addressed the tool could indeed be valuable to life scientists interested in muscle patterning without computational skills.

In our view there are a few limitations, including the accessibility of example data and tutorials at sites.google.com/view/patternj, which we had trouble to access. In addition, we think that the workflow in Fiji, which currently requires pressing several buttons in the correct order, could be further simplified and streamlined by adopting some "wizard" approach, where the user is guided through the steps.

*As answered above, the links on the PatternJ website are now corrected. Regarding the workflow, we now provide a Help menu with:

1. __a basic set of instructions to use the tool, __
2. a direct link to the tutorial video in the PatternJ toolset
3. a direct link to the website on which both the tutorial video and a detailed user manual can be found. We hope this addresses the issues raised by this reviewer.

*Another limitation is the reproducibility of the analysis; here we recommend enabling IJ Macro recording as well as saving of the drawn line ROIs. For more detailed suggestions for improvements please see the above sections of our review. *

We agree that saving ROIs is very useful. It is now implemented in PatternJ.

We are not sure what this reviewer means by "enabling IJ Macro recording". The ImageJ Macro Recorder is indeed very useful, but to our knowledge, it is limited to built-in functions. Our code is open and we hope this will be sufficient for advanced users to modify the code and make it fit their needs.*

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

Summary In this manuscript, the authors present a new toolset for the analysis of repetitive patterns in biological images named PatternJ. One of the main advantages of this new tool over existing ones is that it is simple to install and run and does not require any coding skills whatsoever, since it runs on the ImageJ GUI. Another advantage is that it does not only provide the mean length of the pattern unit but also the subpixel localization of each unit and the distributions of lengths and that it does not require GPU processing to run, unlike other existing tools. The major disadvantage of the PatternJ is that it requires heavy, although very simple, user input in both the selection of the region to be analyzed and in the analysis steps. Another limitation is that, at least in its current version, PatternJ is not suitable for time-lapse imaging. The authors clearly explain the algorithm used by the tool to find the localization of pattern features and they thoroughly test the limits of their tool in conditions of varying SNR, periodicity and band intensity. Finally, they also show the performance of PatternJ across several biological models such as different kinds of muscle cells, neurons and fish embryonic somites, as well as different imaging modalities such as brightfield, fluorescence confocal microscopy, STORM and even electron microscopy.

This manuscript is clearly written, and both the section and the figures are well organized and tell a cohesive story. By testing PatternJ, I can attest to its ease of installation and use. Overall, I consider that PatternJ is a useful tool for the analysis of patterned microscopy images and this article is fit for publication. However, i do have some minor suggestions and questions that I would like the authors to address, as I consider they could improve this manuscript and the tool:

*We are grateful to this reviewer for this very positive assessment of PatternJ and of our manuscript.

* Minor Suggestions: In the methodology section is missing a more detailed description about how the metric plotted was obtained: as normalized intensity or precision in pixels. *

We agree with the reviewer that a more detailed description of the metric plotted was missing. We added this information in the method part and added information in the Figure captions where more details could help to clarify the value displayed.

* The validation is based mostly on the SNR and patterns. They should include a dataset of real data to validate the algorithm in three of the standard patterns tested. *

We validated our tool using computer-generated images, in which we know with certainty the localization of patterns. This allowed us to automatically analyze 30 000 images, and with varying settings, we sometimes analyzed 10 times the same image, leading to about 150 000 selections analyzed. From these analyses, we can provide with confidence an unbiased assessment of the tool precision and the tool capacity to extract patterns. We already provided examples of various biological data images in Figures 4-6, showing all possible features that can be extracted with PatternJ. In these examples, we can claim by eye that PatternJ extracts patterns efficiently, but we cannot know how precise these extractions are because of the nature of biological data: "real" positions of features are unknown in biological data. Such validation will be limited to assessing whether a pattern was found or not, which we believe we already provided with the examples in Figures 4-6.

* The video tutorial available in the PatternJ website is very useful, maybe it would be worth it to include it as supplemental material for this manuscript, if the journal allows it. *

As the video tutorial may have been missed by other reviewers, we agree it is important to make it more prominent to users. We have now added a Help menu in the toolset that opens the tutorial video. Having the video as supplementary material could indeed be a useful addition if the size of the video is compatible with the journal limits.

* An example image is provided to test the macro. However, it would be useful to provide further example images for each of the three possible standard patterns suggested: Block, actin sarcomere or individual band.*

We agree this can help users. We now provide another multi-channel example image on the PatternJ website including blocks and a pattern made of a linear intensity gradient that can be extracted with our simpler "single pattern" algorithm, which were missing in the first example. Additionally, we provide an example to be used with our new time-lapse analysis.

* Access to both the manual and the sample images in the PatternJ website should be made publicly available. Right now they both sit in a private Drive account. *

As mentioned above, we apologize for access issues that occurred during the review process. These files can now be downloaded directly on the website without any sort of authentication. Additionally, these files are now also available on GitHub.

* Some common errors are not properly handled by the macro and could be confusing for the user: When there is no selection and one tries to run a Check or Extraction: "Selection required in line 307 (called from line 14). profile=getProfile( ;". A simple "a line selection is required" message would be useful there. When "band" or "block" is selected for a channel in the "Set parameters" window, yet a 0 value is entered into the corresponding "Number of bands or blocks" section, one gets this error when trying to Extract: "Empty array in line 842 (called from line 113). if ( ( subloc . length == 1 ) & ( subloc [ 0 == 0) ) {". This error is not too rare, since the "Number of bands or blocks" section is populated with a 0 after choosing "sarcomeric actin" (after accepting the settings) and stays that way when one changes back to "blocks" or "bands".*

We thank the reviewer for pointing out these bugs. These bugs are now corrected in the revised version.

* The fact that every time one clicks on the most used buttons, the getDirectory window appears is not only quite annoying but also, ultimately a waste of time. Isn't it possible to choose the directory in which to store the files only once, from the "Set parameters" window?*

We have now found a solution to avoid this step. The user is only prompted to provide the image folder when pressing the "Set parameter" button. We kept the prompt for directory only when the user selects the time-lapse analysis or the analysis of multiple ROIs. The main reason is that it is very easy for the analysis to end up in the wrong folder otherwise.

* The authors state that the outputs of the workflow are "user friendly text files". However, some of them lack descriptive headers (like the localisations and profiles) or even file names (like colors.txt). If there is something lacking in the manuscript, it is a brief description of all the output files generated during the workflow.*

PatternJ generates multiple files, several of which are internal to the toolset. They are needed to keep track of which analyses were done, and which colors were used in the images, amongst others. From the user part, only the files obtained after the analysis All_localizations.channel_X.txt and sarcomere_lengths.txt are useful. To improve the user experience, we now moved all internal files to a folder named "internal", which we think will clarify which outputs are useful for further analysis, and which ones are not. We thank the reviewer for raising this point and we now mention it in our Tutorial.

I don't really see the point in saving the localizations from the "Extraction" step, they are even named "temp".

We thank the reviewer for this comment, this was indeed not necessary. We modified PatternJ to delete these files after they are used.

* In the same line, I DO see the point of saving the profiles and localizations from the "Extract & Save" step, but I think they should be deleted during the "Analysis" step, since all their information is then grouped in a single file, with descriptive headers. This deleting could be optional and set in the "Set parameters" window.*

We understand the point raised by the reviewer. However, the analysis depends on the reference channel picked, which is asked for when starting an analysis, and can be augmented with additional selections. If a user chooses to modify the reference channel or to add a new profile to the analysis, deleting all these files would mean that the user will have to start over again, which we believe will create frustration. An optional deletion at the analysis step is simple to implement, but it could create problems for users who do not understand what it means practically.

* Moreover, I think it would be useful to also save the linear roi used for the "Extract & Save" step, and eventually combine them during the "Analysis step" into a single roi set file so that future re-analysis could be made on the same regions. This could be an optional feature set from the "Set parameters" window. *

We agree with the reviewer that saving ROIs is very useful. ROIs are now saved into a single file each time the user extracts and saves positions from a selection. Additionally, the user can re-use previous ROIs and analyze an image or image series in a single step.

* In the "PatternJ workflow" section of the manuscript, the authors state that after the "Extract & Save" step "(...) steps 1, 2, 4, and 5 can be repeated on other selections (...)". However, technically, only steps 1 and 5 are really necessary (alternatively 1, 4 and 5 if the user is unsure of the quality of the patterning). If a user follows this to the letter, I think it can lead to wasted time.

*

We agree with the reviewer and have corrected the manuscript accordingly (line 119-120).

• *

*I believe that the "Version Information" button, although important, has potential to be more useful if used as a "Help" button for the toolset. There could be links to useful sources like the manuscript or the PatternJ website but also some tips like "whenever possible, use a higher linewidth for your line selection" *

We agree with the reviewer as pointed out in our previous answers to the other reviewers. This button is now replaced by a Help menu, including a simple tutorial in a series of images detailing the steps to follow, a link to the user website, and a link to our video tutorial.

* It would be interesting to mention to what extent does the orientation of the line selection in relation to the patterned structure (i.e. perfectly parallel vs more diagonal) affect pattern length variability?*

As answered to reviewer 1, we understand this concern, which needs to be clarified for readers. The issue may be concerning at first sight, but the errors grow only with the inverse of cosine and are therefore rather low. For example, if the user creates a selection off by 3 degrees, which is visually obvious, lengths will be affected by an increase of only 0.14%. The point raised by the reviewer is important to discuss, and we therefore have added a comment on the choice of selection (lines 94-98) as well as a supplementary figure (Figure 1 - figure supplement 1).

* When "the algorithm uses the peak of highest intensity as a starting point and then searches for peak intensity values one spatial period away on each side of this starting point" (line 133-135), does that search have a range? If so, what is the range? *

We agree that this information is useful to share with the reader. The range is one pattern size. We have modified the sentence to clarify the range of search used and the resulting limits in aperiodicity (now lines 176-181).

* Line 144 states that the parameters of the fit are saved and given to the user, yet I could not find such information in the outputs. *

The parameters of the fits are saved for blocks. We have now clarified this point by modifying the manuscript (lines 186-198) and modifying Figure 1 - figure supplement 5. We realized we made an error in the description of how edges of "block with middle band" are extracted. This is now corrected.

* In line 286, authors finish by saying "More complex patterns from electron microscopy images may also be used with PatternJ.". Since this statement is not backed by evidence in the manuscript, I suggest deleting it (or at the very least, providing some examples of what more complex patterns the authors refer to). *

This sentence is now deleted.

* In the TEM image of the fly wing muscle in fig. 4 there is a subtle but clearly visible white stripe pattern in the original image. Since that pattern consists of 'dips', rather than 'peaks' in the profile of the inverted image, they do not get analyzed. I think it is worth mentioning that if the image of interest contains both "bright" and "dark" patterns, then the analysis should be performed in both the original and the inverted images because the nature of the algorithm does not allow it to detect "dark" patterns. *

We agree with the reviewer's comment. We now mention this point in lines 337-339.

* In line 283, the authors mention using background correction. They should explicit what method of background correction they used. If they used ImageJ's "subtract background' tool, then specify the radius.*

We now describe this step in the method section.

*

Reviewer #3 (Significance (Required)):

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. Being a software paper, the advance proposed by the authors is technical in nature. The novelty and significance of this tool is that it offers quick and simple pattern analysis at the single unit level to a broad audience, since it runs on the ImageJ GUI and does not require any programming knowledge. Moreover, all the modules and steps are well described in the paper, which allows easy going through the analysis.
• Place the work in the context of the existing literature (provide references, where appropriate). The authors themselves provide a good and thorough comparison of their tool with other existing ones, both in terms of ease of use and on the type of information extracted by each method. While PatternJ is not necessarily superior in all aspects, it succeeds at providing precise single pattern unit measurements in a user-friendly manner.
• State what audience might be interested in and influenced by the reported findings. Most researchers working with microscopy images of muscle cells or fibers or any other patterned sample and interested in analyzing changes in that pattern in response to perturbations, time, development, etc. could use this tool to obtain useful, and otherwise laborious, information. *

We thank the reviewer for these enthusiastic comments about how straightforward for biologists it is to use PatternJ and its broad applicability in the bio community.

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

Learn more at Review Commons

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Referee #3

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors present a new toolset for the analysis of repetitive patterns in biological images named PatternJ. One of the main advantages of this new tool over existing ones is that it is simple to install and run and does not require any coding skills whatsoever, since it runs on the ImageJ GUI. Another advantage is that it does not only provide the mean length of the pattern unit but also the subpixel localization of each unit and the distributions of lengths and that it does not require GPU processing to run, unlike other existing tools. The major disadvantage of the PatternJ is that it requires heavy, although very simple, user input in both the selection of the region to be analyzed and in the analysis steps. Another limitation is that, at least in its current version, PatternJ is not suitable for time-lapse imaging.

The authors clearly explain the algorithm used by the tool to find the localization of pattern features and they thoroughly test the limits of their tool in conditions of varying SNR, periodicity and band intensity. Finally, they also show the performance of PatternJ across several biological models such as different kinds of muscle cells, neurons and fish embryonic somites, as well as different imaging modalities such as brightfield, fluorescence confocal microscopy, STORM and even electron microscopy.

This manuscript is clearly written, and both the section and the figures are well organized and tell a cohesive story. By testing PatternJ, I can attest to its ease of installation and use. Overall, I consider that PatternJ is a useful tool for the analysis of patterned microscopy images and this article is fit for publication. However, i do have some minor suggestions and questions that I would like the authors to address, as I consider they could improve this manuscript and the tool:

Minor Suggestions:

In the methodology section is missing a more detailed description about how the metric plotted was obtained: as normalized intensity or precision in pixels. The validation is based mostly on the SNR and patterns. They should include a dataset of real data to validate the algorithm in three of the standard patterns tested. The video tutorial available in the PatternJ website is very useful, maybe it would be worth it to include it as supplemental material for this manuscript, if the journal allows it. An example image is provided to test the macro. However, it would be useful to provide further example images for each of the three possible standard patterns suggested: Block, actin sarcomere or individual band. Access to both the manual and the sample images in the PatternJ website should be made publicly available. Right now they both sit in a private Drive account. Some common errors are not properly handled by the macro and could be confusing for the user: When there is no selection and one tries to run a Check or Extraction: "Selection required in line 307 (called from line 14). profile=getProfile( <)>;". A simple "a line selection is required" message would be useful there. When "band" or "block" is selected for a channel in the "Set parameters" window, yet a 0 value is entered into the corresponding "Number of bands or blocks" section, one gets this error when trying to Extract: "Empty array in line 842 (called from line 113). if ( ( subloc . length == 1 ) & ( subloc [ 0 <]> == 0) ) {". This error is not too rare, since the "Number of bands or blocks" section is populated with a 0 after choosing "sarcomeric actin" (after accepting the settings) and stays that way when one changes back to "blocks" or "bands".<br /> The fact that every time one clicks on the most used buttons, the getDirectory window appears is not only quite annoying but also, ultimately a waste of time. Isn't it possible to choose the directory in which to store the files only once, from the "Set parameters" window? The authors state that the outputs of the workflow are "user friendly text files". However, some of them lack descriptive headers (like the localisations and profiles) or even file names (like colors.txt). If there is something lacking in the manuscript, it is a brief description of all the output files generated during the workflow. I don't really see the point in saving the localizations from the "Extraction" step, they are even named "temp". In the same line, I DO see the point of saving the profiles and localizations from the "Extract & Save" step, but I think they should be deleted during the "Analysis" step, since all their information is then grouped in a single file, with descriptive headers. This deleting could be optional and set in the "Set parameters" window. Moreover, I think it would be useful to also save the linear roi used for the "Extract & Save" step, and eventually combine them during the "Analysis step" into a single roi set file so that future re-analysis could be made on the same regions. This could be an optional feature set from the "Set parameters" window. In the "PatternJ workflow" section of the manuscript, the authors state that after the "Extract & Save" step "(...) steps 1, 2, 4, and 5 can be repeated on other selections (...)". However, technically, only steps 1 and 5 are really necessary (alternatively 1, 4 and 5 if the user is unsure of the quality of the patterning). If a user follows this to the letter, I think it can lead to wasted time. I believe that the "Version Information" button, although important, has potential to be more useful if used as a "Help" button for the toolset. There could be links to useful sources like the manuscript or the PatternJ website but also some tips like "whenever possible, use a higher linewidth for your line selection" It would be interesting to mention to what extent does the orientation of the line selection in relation to the patterned structure (i.e. perfectly parallel vs more diagonal) affect pattern length variability? When "the algorithm uses the peak of highest intensity as a starting point and then searches for peak intensity values one spatial period away on each side of this starting point" (line 133-135), does that search have a range? If so, what is the range? Line 144 states that the parameters of the fit are saved and given to the user, yet I could not find such information in the outputs. In line 286, authors finish by saying "More complex patterns from electron microscopy images may also be used with PatternJ.". Since this statement is not backed by evidence in the manuscript, I suggest deleting it (or at the very least, providing some examples of what more complex patterns the authors refer to). In the TEM image of the fly wing muscle in fig. 4 there is a subtle but clearly visible white stripe pattern in the original image. Since that pattern consists of 'dips', rather than 'peaks' in the profile of the inverted image, they do not get analyzed. I think it is worth mentioning that if the image of interest contains both "bright" and "dark" patterns, then the analysis should be performed in both the original and the inverted images because the nature of the algorithm does not allow it to detect "dark" patterns. In line 283, the authors mention using background correction. They should explicit what method of background correction they used. If they used ImageJ's "subtract background' tool, then specify the radius.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. Being a software paper, the advance proposed by the authors is technical in nature. The novelty and significance of this tool is that it offers quick and simple pattern analysis at the single unit level to a broad audience, since it runs on the ImageJ GUI and does not require any programming knowledge. Moreover, all the modules and steps are well described in the paper, which allows easy going through the analysis.
• Place the work in the context of the existing literature (provide references, where appropriate). The authors themselves provide a good and thorough comparison of their tool with other existing ones, both in terms of ease of use and on the type of information extracted by each method. While PatternJ is not necessarily superior in all aspects, it succeeds at providing precise single pattern unit measurements in a user-friendly manner.
• State what audience might be interested in and influenced by the reported findings. Most researchers working with microscopy images of muscle cells or fibers or any other patterned sample and interested in analyzing changes in that pattern in response to perturbations, time, development, etc. could use this tool to obtain useful, and otherwise laborious, information.
• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. I am a biologist with extensive experience in confocal microscopy and image analysis using classical machine vision tools, particularly using ImageJ and CellProfiler.

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Referee #2

Evidence, reproducibility and clarity

Summary

The authors present an ImageJ Macro GUI tool set for the quantification of one-dimensional repeated patterns that are commonly occurring in microscopy images of muscles.

Major comments

In our view the article and also software could be improved in terms of defining the scope of its applicability and user-ship. In many parts the article and software suggest that general biological patterns can be analysed, but then in other parts very specific muscle actin wordings are used. We are pointing this out in the "Minor comments" sections below. We feel that the authors could improve their work by making a clear choice here. One option would be to clearly limit the scope of the tool to the analysis of actin structures in muscles. In this case we would recommend to also rename the tool, e.g. MusclePatternJ. The other option would be to make the tool about the generic analysis of one-dimensional patterns, maybe calling the tool LinePatternJ. In the latter case we would recommend to remove all actin specific wordings from the macro tool set and also the article should be in parts slightly re-written.

Minor/detailed comments

Software

We recommend considering the following suggestions for improving the software.

File and folder selection dialogs

In general, clicking on many of the buttons just opens up a file-browser dialog without any further information. For novel users it is not clear what the tool expects one to select here. It would be very good if the software could be rewritten such that there are always clear instructions displayed about which file or folder one should open for the different buttons.

Extract button

The tool asks one to specify things like whether selections are drawn "M-line-to-M-line"; for users that are not experts in muscle morphology this is not understandable. It would be great to find more generally applicable formulations.

Manual selection accuracy

The 1st step of the analysis is always to start from a user hand-drawn profile across intensity patterns in the image. However, this step can cause inaccuracy that varies with the shape and curve of the line profile drawn. If not strictly perpendicular to for example the M line patterns, the distance between intensity peaks will be different. This will be more problematic when dealing with non-straight and parallelly poised features in the image. If the structure is bended with a curve, the line drawn over it also needs to reproduce this curve, to precisely capture the intensity pattern. I found this limits the reproducibility and easy-usability of the software.

Reproducibility

Since the line profile drawn on the image is the first step and very essential to the entire process, it should be considered to save together with the analysis result. For example, as ImageJ ROI or ROIset files that can be re-imported, correctly positioned, and visualized in the measured images. This would greatly improve the reproducibility of the proposed workflow. In the manuscript, only the extracted features are being saved (because the save button is also just asking for a folder containing images, so I cannot verify its functionality).

? button

It would be great if that button would open up some usage instructions.

Easy improvement of workflow

I would suggest a reasonable expansion of the current workflow, by fitting and displaying 2D lines to the band or line structure in the image, that form the "patterns" the author aims to address. Thus, it extracts geometry models from the image, and the inter-line distance, and even the curve formed by these sets of lines can be further analyzed and studied. These fitted 2D lines can be also well integrated into ImageJ as Line ROI, and thus be saved, imported back, and checked or being further modified. I think this can largely increase the usefulness and reproducibility of the software.

Manuscript

We recommend considering the following suggestions for improving the manuscript. Abstract: The abstract suggests that general patterns can be quantified, however the actual tool quantifies specific subtypes of one-dimensional patterns. We recommend adapting the abstract accordingly.

Line 58: Gray-level co-occurrence matrix (GLCM) based feature extraction and analysis approach is not mentioned nor compared. At least there's a relatively recent study on Sarcomeres structure based on GLCM feature extraction: https://github.com/steinjm/SotaTool with publication: https://doi.org/10.1002/cpz1.462

Line 75: "...these simple geometrical features will address most quantitative needs..." We feel that this may be an overstatement, e.g. we can imagine that there should be many relevant two-dimensional patterns in biology?!

Line 83: "After a straightforward installation by the user, ...". We think it would be convenient to add the installation steps at this place into the manuscript.

Line 87: "Multicolor images will give a graph with one profile per color." The 'Multicolor images' here should be more precisely stated as "multi-channel" images. Multi-color images could be confused with RGB images which will be treated as 8-bit gray value (type conversion first) images by profile plot in ImageJ.

Line 92: "...such as individual bands, blocks, or sarcomeric actin...". While bands and blocks are generic pattern terms, the biological term "sarcomeric actin" does not seem to fit in this list. Could a more generic wording be found, such as "block with spike"?

Line 95: "the algorithm defines one pattern by having the features of highest intensity in its centre". Could this be rephrased? We did not understand what that exactly means.

Line 124 - 147: This part the only description of the algorithm behind the feature extraction and analysis, but not clearly stated. Many details are missing or assumed known by the reader. For example, how it achieved sub-pixel resolution results is not clear. One can only assume that by fitting Gaussian to the band, the center position (peak) thus can be calculated from continuous curves other than pixels.

Line 407: We think the availability of both the tool and the code could be improved. For Fiji tools it is common practice to create an Update Site and to make the code available on GitHub. In addition, downloading the example file (https://drive.google.com/file/d/1eMazyQJlisWPwmozvyb8VPVbfAgaH7Hz/view?usp=drive_link) required a Google login and access request, which is not very convenient; in fact, we asked for access but it was denied. It would be important for the download to be easier, e.g. from GitHub or Zenodo.

Significance

The strength of this study is that a tool for the analysis of one-dimensional repeated patterns occurring in muscle fibres is made available in the accessible open-source platform ImageJ/Fiji. In the introduction to the article the authors provide an extensive review of comparable existing tools. Their new tool fills a gap in terms of providing an easy-to-use software for users without computational skills that enables the analysis of muscle sarcomere patterns. We feel that if the below mentioned limitations could be addressed the tool could indeed be valuable to life scientists interested in muscle patterning without computational skills.

In our view there are a few limitations, including the accessibility of example data and tutorials at sites.google.com/view/patternj, which we had trouble to access. In addition, we think that the workflow in Fiji, which currently requires pressing several buttons in the correct order, could be further simplified and streamlined by adopting some "wizard" approach, where the user is guided through the steps. Another limitation is the reproducibility of the analysis; here we recommend enabling IJ Macro recording as well as saving of the drawn line ROIs. For more detailed suggestions for improvements please see the above sections of our review.

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Referee #1

Evidence, reproducibility and clarity

I have trialled the package on my lab's data and it works as advertised. It was straightforward to use and did not require any special training. I am confident this is a tool that will be approachable even to users with limited computational experience. The use of artificial data to validate the approach - and to provide clear limits on applicability - is particularly helpful.

The main limitation of the tool is that it requires the user to manually select regions. This somewhat limits the generalisability and is also more subjective - users can easily choose "nice" regions that better match with their hypothesis, rather than quantifying the data in an unbiased manner. However, given the inherent challenges in quantifying biological data, such problems are not easily circumventable.

I have some comments to clarify the manuscript:

1. A "straightforward installation" is mentioned. Given this is a Method paper, the means of installation should be clearly laid out.
2. It would be helpful if there was an option to generate an output with the regions analysed (i.e., a JPG image with the data and the drawn line(s) on top). There are two reasons for this: i) A major problem with user-driven quantification is accidental double counting of regions (e.g., a user quantifies a part of an image and then later quantifies the same region). ii) Allows other users to independently verify measurements at a later time.
3. Related to the above point, it is highlighted that each time point would need to be analysed separately (line 361-362). It seems like it should be relatively straightforward to allow a function where the analysis line can be mapped onto the next time point. The user could then adjust slightly for changes in position, but still be starting from near the previous timepoint. Given how prevalent timelapse imaging is, this seems like (or something similar) a clear benefit to add to the software.
4. Line 134-135. The level of accuracy of the searching should be clarified here. This is discussed later in the manuscript, but it would be helpful to give readers an idea at this point what level of tolerance the software has to noise and aperiodicity.

Referees cross-commenting

I think the other reviewer comments are very pertinent. The authors have a fair bit to do, but they are reasonable requests. So, they should be encouraged to do the revisions fully so that the final software tool is as useful as possible.

Significance

Developing software tools for quantifying biological data that are approachable for a wide range of users remains a longstanding challenge. This challenge is due to: (1) the inherent problem of variability in biological systems; (2) the complexity of defining clearly quantifiable measurables; and (3) the broad spread of computational skills amongst likely users of such software.

In this work, Blin et al., develop a simple plugin for ImageJ designed to quickly and easily quantify regular repeating units within biological systems - e.g., muscle fibre structure. They clearly and fairly discuss existing tools, with their pros and cons. The motivation for PatternJ is properly justified (which is sadly not always the case with such software tools).

Overall, the paper is well written and accessible. The tool has limitations but it is clearly useful and easy to use. Therefore, this work is publishable with only minor corrections.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

The manuscript by Barba-Aliaga and colleagues describe a potential function of eIF5A for the control of TIM50 translation. The authors showed that in temperature-sensitive mutants of eIF5A several mitochondrial proteins are decreased including OXPHOS subunits, proteins of the TCA cycle and some components of protein translocases. Some precursor proteins appear to localize into the cytosol. As consequent of mitochondrial dysfunction, the expression of some stress components is induced. The idea is that eIF5A ribosome-stalling of the proline-rich Tim50 of the TIM23 complex and thereby controls mitochondrial protein set-up.

The findings are potentially interesting. However, some control experiments are required to substantiate the findings.

1. To support their conclusion the authors should show whether Tim50 levels are affected in the eIF5A-ts mutants used. Tim50 protein half-life is approximately 9.6 h (Christiano et al, 2014), which makes difficult to measure large differences in new protein synthesis upon eIF5A depletion. However, we used different approaches to show that reduction in eIF5A provokes a reduction in Tim50 protein levels and synthesis. 1) The steady-state levels of Tim50 protein (genomic HA-tagged version) are shown by western blotting analysis in Fig. S4B and confirm a significant drop of approximately 20% in the tif51A-1 mutant at restrictive temperature. 2) The use of a construct in which Tim50 is fused to a nanoluciferase reporter under the control of a tetO7 inducible promoter shows a significant 3-fold reduction in Tim50 protein synthesis in the tif51A-1 mutant compared to wild-type (Fig. 4C). In addition, the protein synthesis time is calculated and indicates that it takes the double time for the tif51A-1 strain to synthesize Tim50 protein than the wild-type (Fig. 4E). 3) The expression of a FLAG-TIM50-GFP version under a GAL inducible system also shows a significant reduction in Tim50 protein synthesis in the two eIF5A temperature-sensitive strains (Fig. S4C). 4) The proteomic analysis performed at 41ºC showed a 20% reduction in Tim50 protein levels in the two eIF5A temperature-sensitive strains, although not being statistically significant (Table S1). Furthermore, TIM50 mRNA levels were determined by RT-qPCR across all the experiments mentioned to confirm that the low levels of Tim50 protein were not due to decreased transcription or increased mRNA degradation. 5) An additional experiment of polysome profiling has been included in Fig. R1 (Figure for Reviewers) showing a higher TIM50 mRNA abundance at low polysomal fractions and a lower mRNA abundance at heavy polysomal fractions upon eIF5A depletion. This indicates that the TIM50 mRNA abundance is significantly shifted to earlier fractions and translation of Tim50 is reduced in the tif51A-1 mutant at restrictive temperature but not at permissive temperature. Altoghether, all these experiments confirm a significant reduction of Tim50 protein levels upon eIF5A depletion and conclusions are supported on these results.

How are the levels of TOM and TIM23 subunits?

Response: Our proteomic analysis shows that the protein levels of Tom70 and Tom20 receptor subunits of the TOM complex are significantly decreased in the two eIF5A temperature-sensitive strains (Table S1). These results are in agreement with the polysome profiling results, where it is seen a significant reduction of TOM70 and TOM20 mRNAs in the heavy polysomal fractions while a significant increase of these mRNAs is observed in the light fractions of eIF5A-depleted cells (Fig. 2C and Fig. S2D). Apart from Tim50, no other proteins of the Tim23 translocase complex were detected in the proteomic analysis.

Furthermore, how are the levels of the Tim50 variant that lack the proline residues? Is the stability or function of Tim50 affected by these mutations?

Although we did not specifically analysed the Tim50ΔPro protein levels, a quantification of the Tim50ΔPro fluorescent signal has been performed to address this matter and is shown in Fig. R2 and mentioned in the corresponding Results section. Results indicate that the Tim50 variant lacking the proline residues has similar protein levels to the wild-type version and therefore, it is tempting to say that its stability should also be similar. However, if Reviewers consider this to be essential for publishing, additional experiments using cycloheximide could be conducted in order to better assess the stability and half-life of this Tim50 version.

Additionally, functional levels of Tim50ΔPro protein is shown by the fact that wild-type cells carrying this Tim50 protein version as the only copy of Tim50 grew well in glycerol media, where Tim50 is essential for the mitochondrial function (Fig. 5A). However, we suspect that Tim50ΔPro is a bit less efficient protein since a double mutant tif51A-1 Tim50ΔPro shows even reduced growth than the single tif51A-1 mutant (Fig. 5A). This information also responds to the comments made by Reviewer #2.

How specific is the effect of eIF5A on Tim50? Is there any other mitochondrial substrate of eIF5A? It is not so clear to the reviewer why the authors focused on Tim50.

Response: eIF5A has been shown to be necessary for the translation of mRNA codons encoding for consecutive prolines and, consequently, lack of eIF5A causes ribosome stalling in these polyproline motifs (Gutierrez et al., 2013; Pelechano and Alepuz, 2017; Schuller et al., 2017). In our manuscript we showed: 1) using an artificial tetO7-TIM50-nanoLuc genomic construct we demonstrate that the synthesis of Tim50 protein (measured as appearance of luciferase activity upon induction of tetO promoter) is significantly reduced by 3-fold under eIF5A depletion only when Tim50 contains the stretch of 7 consecutive prolines (Fig. 4A-D); 2) genomic Tim50-HA and plasmid FLAG-TIM50-GFP protein levels are significantly reduced upon eIF5A depletion (Fig. S4B); 3) calculation of the time for translation elongation of Tim50 mRNA shows that this time is double in cells with eIF5A depletion than in cells containing normal eIF5A levels (Fig. 4E); and 4) analysis of published ribosome profiling data shows a precipitous drop-off in ribosome density exactly where the stretch of polyprolines is located in Tim50 (540-561bp) upon eIF5A depletion but not in the control strain (Fig. 4F). This result is indicative of ribosome stalling at Tim50 polyproline motif upon eIF5A depletion. Altogether, our results strongly support a direct and specific role of eIF5A in Tim50 protein synthesis. However, as we discuss in relation to Fig. 5 and in the Discussion section, Tim50 does not seem to be the only mitochondrial substrate of eIF5A, since recovery of Tim50 protein synthesis does not rescue the growth of eIF5A mutants under respiratory conditions. In this line, we have added further data pointing to ribosome stalling for other co-translationally inserted mitoproteins which are potential substrates of eIF5A (Table S6). Accordingly, this has also been included in the Discussion section. This information also responds to the comments made by Reviewer #4.

Our focus on Tim50 in this manuscript resides in that we found a global downregulation of mitochondrial protein synthesis (Fig.1 and 2) in parallel to the accumulation of mitochondrial precursor proteins in the cytoplasm and induction of the mitoCPR response (Fig.3). All these data were pointing to a mitochondrial protein import defect. Since Tim50 is an essential component of the Tim23 translocase complex, its protein levels are reduced in eIF5A mutants and Tim50 contains a polyproline motif, all these data were pointing towards a Tim50-dependent effect in mitochondrial protein import upon eIF5A depletion, which we addressed in the manuscript.

Figure 1A: Which tif51A strain was used?

Response: The proteomic analysis was performed with tif51A-1 and tif51A-3 temperature-sensitive strains (see Table S1) and Fig.1A shows the average of the values obtained for the two mutants (proteins detected as down-regulated in these two samples and from 3 different biological replicates). This is now clarified in the Figure 1A legend. A similar approach was also followed in Pelechano and Alepuz, 2017. Additionally, the ratios between the protein level in the temperature-sensitive mutant respect wild-type for each protein and for each eIF5A mutant are also shown in Table S1. This information also responds to the comments made by Reviewer #2.

Figure 1C: The authors should show the steady state levels of some OXPHOS/TCA components to confirm the findings of Figure 1A.

Response: Proteomic findings have been confirmed for several proteins. The steady state levels of Por1 and Hsp60 proteins were investigated by western blotting (Figs. 1C,D) and results show a significant down-regulation on the two eIF5A temperature-sensitive strains at 41ºC, which confirms the findings of Fig. 1A. Additionally, we have included the same experiment performed at 37ºC (Fig. S1E), which also confirms the same conclusion.

Furthermore, the steady-state levels of Tim50 protein were also investigated by western blotting (Fig. S4B), and results also showed a significant down-regulation in the tif51A-1 mutant at restrictive temperature (37ºC), compared to wild-type. This result also confirms the findings of Fig. 1A.

However, if Reviewers consider that additional confirmation for OXPHOS/TCA proteins to be essential for publishing, additional experiments could be conducted to assess the protein levels of other OXPHOS/TCA proteins.

The manuscript contains several quantifications. However, central information like number of repeats or whether a standard deviation or S.E.M. is depicted are missing.

Response: Clear information on the number of repeats, type of graphical representation and statistical analysis is now included for all figures in the corresponding figure legends and also detailed in the Materials and Methods section. This information also responds to the comments made by Reviewer #2.

Figure 3: The authors propose that precursor form aggregates outside mitochondria. To assess the data, a quantification should address in how many cells are protein aggregates.

Response: The quantification of cytoplasmic Yta12 aggregates is now included in Fig.3E, which shows significant differences between the tif51A-1 mutant and the wild-type strain. In addition, quantification of cytosolic Tim50 aggregates was already included in Fig. 4H, which also shows significant differences between the tif51A-1 mutant and the wild-type strain. These two figures include the individual values from three biological replicates (at least 150 cells were analyzed), mean, standard deviation and statistical analysis.

Do the observed aggregated proteins interact with Hsp104? recycled?

Response: Yes, the cytoplasmic mitochondrial precursor aggregated proteins co-localize with Hsp104 as shown in Fig. 3I for Cyc1 and in Fig. 4J for Tim50. The quantification of Cyc1 and Tim50 co-localization with Hsp104 is shown in Fig S5D.

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Significance

See above

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Reviewer #2

Evidence, reproducibility and clarity

The authors report here novel findings concerning the role of eIF5A in mediating protein import to mitochondria in the model eukaryote Saccharomyces cerevisiae. It was previously known from structural and other studies that the translation factor eIF5A binds to the E-site of stalled ribosomes to help promote peptide bond formation. It was inferred by ribosome footprinting and reporter studies assessing the impact of eIF5A depletion that eIF5A is particularly needed to translate several specific amino acid motifs including polyproline stretches. However additional target sequences are known.

Here a proteomics approach reveals clear evidence that mitochondrially targeted proteins are impacted by temperature sensitive mutations in eIF5A that deplete the factor, including those without polyprolines. The authors then use a range of molecular and cell biology to focus on the role of mitochondrial signal sequences/mitochondrial protein import and the mitochondrial stress response, before highlighting a role for poly-prolines in Tim50, a major mitochondrial protein import factor. Consistent with the ribosome footprinting done previously it is shown that a stretch of 7 prolines limit its translation when eIF5A is depleted and studies shown here are consistent with the idea that this has wider consequences for mitochondrial protein import and hence translation/stability of other proteins. However improved Tim50 translation alone, by eliminating the poly-proline motif, is not sufficient to overcome all consequences of eIF5A depletion for mitochondrial protein import and for viability, suggesting a wider role.

In general the text flows nicely, this could be a study that explains why a large number of mitochondrially targeted proteins are impacted by depletion of eIF5A in yeast. As the poly Pro sequence in Tim50 is not conserved in higher eukaryotes it is unclear how this observation will scale to other systems, but it provides an example of how studies in a relatively simple system can trace wide-spread impact of the loss of one component of a central pathway-here protein synthesis to altered translation of a key component of another process-mitochondrial protein import. Given that eIF5A and its hypusine modifying enzymes are mutated in rare human disorders, it is likely there will be interest in this study.

However, while the conclusions may be justified, there are significant deficiencies in how the experiments have been analysed and presented in this version of the manuscript that impact every figure shown, coupled with deficiencies in the methods section that all need to be addressed. Thus, we have here the basis of what should be a very interesting paper here, but there is a lot of work to do to remedy perceived weaknesses. It may be that the overall conclusions are entirely sound and appropriate, but I suspect that performing the statistics in less biased ways may change some of the significant differences claimed. Some explanations concerning how data analyses were conducted and the reasons for specific analysis decisions being made would also improve the narrative. These points are expanded on below.

All the edits suggested here are aimed at improving the rigor of reporting in this study. Depending on how they are answered some may become major issues, or they could all be minor.

1 Figure 1 shows proteomic data for response to heat shock at 41{degree sign}C. In the text it is made clear that two different temperature sensitive missense alleles the 51A-1 and 51A-3 were analysed, but the single volcano plot in Figure 1A does not say whether it is reporting one of these experiments compared to WT (which one) or some other analysis (ie have data from the 2 mutants been amalgamated somehow?). I would assume only one, but which one, and why only one plot? How different is the other experiment? Why does the Figure title say the experiment is an eIF5A deletion when it is not this?

Response: The data shown in Figure 1A corresponds to the average values obtained in the proteomic analysis for the two temperature-sensitive mutants tif51A-1 and tif51A-3 (with data for each mutant obtained from 3 different biological replicates). Highly reproducible proteomic results and similar between the two mutants were obtained (see in Fig. S1A the MDS-plot showing all replicates for each strain and condition studied in the proteomic analysis). In addition, the proteomic data showing the protein 41°C/25°C ratio for each eIF5A temperature-sensitive mutant with respect to wild-type is shown in the Table S1. This is now clarified in the Figure 1A legend. A similar approach using the mean values of the two mutants was followed in the analysis of ribosome footprintings made in Pelechano and Alepuz, 2017. Additionally, the ratios between the protein level in the temperature-sensitive mutant respect wild-type for each protein and for each eIF5A mutant are also shown in Table S1. This information also responds to the comments made by Reviewer #1.

Reviewer #2 is right with his/her comment and there was a mistake in the Fig.1 title. Now it is corrected and written “depletion” instead of the wrong “deletion”.

2 Why were the experiments shown in Figure 1 done at 41{degree sign}C when all other experiments are done at 37{degree sign}C? This experimental difference is ignored in the text and no comparison of the impact of 37 vs 41 is made anywhere in the manuscript. For example it would be straightforward to perform a comparison of eIF5A depletion (by western blot), polyribosome profiles, strain growth/inhibition at both temperatures.

Response: Our aim carrying out a proteomic experiment after 4 hours of incubation of the temperature-sensitive strains at 41°C was to get a more profound depletion of the eIF5A protein, which is very abundant and stable at normal conditions, in order to get clear proteomic results. The proteomic results were pointing to a reduction in the levels of many mitochondrial proteins, corroborating previous results obtained in murine embryonic fibroblasts upon depletion of active eIF5A conditions (https://doi.org/10.1016/j.cmet.2019.05.003). From this starting point we tried to find out the molecular mechanism involved and all the rest of experiments are done with temperature sensitive eIF5A mutants under restrictive temperature of 37°C that is the most common conditions used in yeast by us and others, and in which wild-type yeast cells still grow vigorously.

In our previous manuscript version, the depletion of eIF5A after growing the cells at 41ºC for 4 h was shown in Fig. 1C. These data has been expanded and we have now included in Fig. S1E a western blotting analysis that shows the depletion of eIF5A after incubating the cells at 37ºC and 41 ºC for 4 h (Fig. S1E). The steady state level of the mitochondrial Por1 protein was investigated by western blotting (Figs. 1C,D) and results show a significant down-regulation in the two eIF5A temperature-sensitive strains at 41ºC. We have now included the same experiment performed at 37ºC (Fig. S1E), which also confirms the same conclusion. In addition, following Reviewer #2 suggestions, growth of the wild-type and tif51A-1 strains was tested by serial drop assays conducted at 25ºC, 37ºC and 41ºC and results confirm that both 37ºC and 41ºC temperatures impair the growth of the tif51A-1 strain but not the wild-type (Fig.S1B). The new information included in Figure S1 is now explained in the Results section. This information also responds to the comments made by Reviewer #4.

3 Western blot quantification. In Figure 1D and E the authors present western blot quantification. However they have chosen to normalise every panel to the signal in lane 1. This means that there is no variation at all in that sample as every replicate is =1. This completely skews the statistical assumptions made (because there will be variation in that sample) and effectively invalidates all the statistics shown. An appropriate approach to use is to normalise the signal in each lane to the mean signal across all lanes in a single blot. That way if all are identical they remain at 1, but importantly variation across all samples is captured. This should be done to the loading controls as well before working out ratios or performing any statistical analyses.

Response: Following Reviewer #2 suggestions we have changed the normalization methodology for the Western blots and we have now normalized the signal in each lane to the mean signal across all lanes in each single blot, and do so also for the loading controls. We have conducted this analysis in every western blotting experiment shown in the manuscript (Figs. 1D, S4B and S4C) and statistical analyses have been performed again to capture variation across all samples. In addition, this is also included in the Materials and Methods section (“Western blotting” subsection). Results obtain are similar to previous ones but we agree that this new approach improves the data presentation.

For this type of experiment it is more appropriate to use Anova than a T-test. This advice applies to every western data analysis figure in the whole manuscript and so all associated statistics need to be done again from the original quantification values. If T-test is justified then a correction for multiple hypothesis testing should be applied.

Response: After reviewing a large number of publications analysing similar data, and also following the recommendations of our statistical department, we have retained the statistics used in our previous version (with the new data normalisation as explained above, following the recommendations of Reviewer #2). This is because for each western blot figure shown, we have performed experiments with two different biological samples, wild-type cells and eIF5A mutant cells, and compared results for a single variable (Por1 protein level; eIF5A protein level or Hsp60 protein level) using three or more biological replicates. In this context, we compare the mean of the protein levels obtained from the biological replicate for two groups: wild-type and eIF5A mutant. Therefore, we believe that the statistical T-test is more appropriate. However, we could repeat the statistic if it is finally considered more appropriate.

In all bar chart figures in addition to showing the mean and SD, each replicate value should be shown (eg as done in Fig 2C). Graphpad allows individual points to be plotted easily.

Response: All Figures along the manuscript now include individual values from each replicate, in addition to showing the mean, SD and statistical analysis. All figure legends have been corrected accordingly.

5 Figure 2. Polysome profiles. The impact of translation elongation stalls on global polysome profiles is complex, but a global run off is highly unlikely. Stalls later in the coding region would be anticipated to cause an increase in ribosome density as more ribosomes accumulate (like cars queueing held at a red light). However where a stall is early in a longer ORF, for example at a signal sequence, then there is less opportunity for ribosomes to join and so for those mRNAs moving to lighter points in the gradient may be observed. This may also cause knock on effects on AUG clearance and initiation which the authors appear to see as there may be an increased 60S peak in the traces shown. Are there differences in overall -low vs high polysomes, the traces shown suggest there may be? Discussion of these points is merited in the results section given the subsequent qPCR experiment.

Response: The comments made by the Reviewer #2 are very interesting and we have made changes accordingly. First, we now show in Fig. 2A,B and Fig.S2B,C the quantification of polysomal and monosomal fractions in wild-type and tif51A-1 mutants at permissive and restrictive temperatures. It can be appreciated that there is no impact on global polysomal and monosomal fractions under eIF5A depletion. This result does not support a global stall at 3’ region of the ORF, because then an increase in polysomal fractions should be detected; nor a global stall at the 5’ region of the ORF, because then a decrease in polysomal fractions should be detected. However, with respect to individual mRNAs, our data show a significant reduction in the heavier polysomal fractions and a significant increase in lighter polysomal fractions for mRNAs encoding mitochondrial proteins, while no significant changes were observed for mRNAs encoding cytoplasmic proteins (Fig. 2C and Fig. S2D-I). These results could be interpreted as a result of ribosome stalls in the 5’ ORF regions, for example at the signal sequence, according to Reviewer #2 comments.

We have now introduced this comment in the Results and Discussion sections.

Figure 2 qPCR. Using qPCR to analyse RNA levels across polysome gradients is tricky for multiple reasons including that the total RNA level varies across fractions that can impact recovery efficiencies following precipitation of gradient fractions. Often investigators use a spike in control to act as a normalising factor. Here it is completely unclear what analysis was done because details are not stated anywhere. How were primers optimized, was amplification efficiency determined? Or are they assumed to be 100%, which they will not be? A detailed description or reference to a study where that is written is needed.

Response: The RNA extraction and analyses by RT-qPCR of the mRNA levels in the polysomal gradients was done as in previous studies of our lab (Romero et al. Sci Rep. 2020;10(1):233. doi: 10.1038/s41598-019-57132-0; Ramos-Alonso et al. PLoS Genet. 2018;14(6):e1007476. doi: 10.1371/journal.pgen.1007476; van Wijlick et al. PLoS Genet. 2016;12(10):e1006395. doi: 10.1371/journal.pgen.1006395; Garre et al., 2012 Mol Biol Cell. ;23(1):137-50. doi: 10.1091/mbc.E11-05-0419.). Three independent replicates were analyzed and results were reproducible and statistically significant, as shown in Fig. S2. Total RNA was extracted from each fraction using the SpeedTools Total RNA Extraction kit (Biotools B&M Labs). In the first replicate a spike in RNA control (Phenylalanine) was added and tested that no significant differences in the results were obtained when using or not the spike in control (see below Figure R3 for referees). mRNA relative values are always obtained from qPCR using a calibrating efficiency standard curve for each pair of oligos, after the initial set up of the qPCR for this specific pair of oligos. Therefore, slight differences in amplification efficiencies for each oligo pair are taken into account. More details about qPCR are now included in the Materials and Methods section (“Polyribosome profile analysis” subsection) and one additional reference is also included for the processing of polysomal gradient fractions.

It would be helpful to state how long CDS are for these mRNAs and where 2-3/2-8 cut off made is what for determining what is 'short' vs 'long' and the scientific basis for selecting 2-3 vs 2-8, why 8? Were M fractions also used in qPCR, they appear to be ignored in the analysis as currently presented?

Response: The CDS lengths of the mRNAs analyzed by polysome profiling and other important features are now included in new Table S5. We decided to classify as short length mRNAs those with a length below 600 bp, while mRNAs with lengths above 600 bp were classified as long length mRNAs. This classification was made on the basis of specific mRNA profiles obtained by qPCR analysis. mRNAs with short lengths behaved similarly and we selected 2n-3n fractions since the main polysomal peak under normal conditions appeared among 4n-5n fractions. In this line, long length mRNAs also behaved similarly between them, and we selected 2n to 8n fractions since the main polysomal peak under normal conditions appeared right after the 8n fraction. This information is now included in the Results and Materials and Methods sections.

Regarding the use of the Monosomal fractions, yes, they were used as it can be seen in Fig. S2 which includes the distribution in Monosomal (M), lighter (2n-3n/2n-8n) or heavier (n>3/n>8, P) polysomal fractions. In the polysomal profiles we can be see that depletion of eIF5A causes a reduction in the amount of mitochondrial mRNAs in the heavier fractions and a corresponding increase in the amount of mRNAs in the lighter polysomal fractions, while no significant changes are found in the monosomal fractions. Therefore, the statistically significant change in the heavier/lighter polysomal fraction ratio is indicative of the translation down-regulation and these ratios are shown in Fig. 2C. As the Reviewer #2 commented in point 5, the change in mRNA distribution to lighter polysomal fractions may be indicative or ribosome stalling at the 5’ ORF region, compatible with a stall at the mitochondrial target signal (MTS), and this discussion is now included in the Results and Discussion section.

Which transcripts studied here encode proteins with signal sequences? As Signal sequence pauses early in translation should impact ribosome loading this is potentially important here as discussed above.

Response: Yes, we agree with Reviewer #2 that this information may be relevant according to the hypothesis of ribosome stall at the MTS. Therefore, a score value of probability of harbouring an MTS presequence (Fukasawa et al., 2015) is now included in Table S5 for each of the mRNAS analyzed by polysome profiling. The discussion of this point has also been included in the Results and Discussion sections.

While it has been shown that SRP recognition is able to slow and even arrest translation of ER signal recognition peptides, there is currently no known direct SRP like correlate for mitochondrial signal sequences. We are therefore unaware of literature showing that mitochondrial signal sequences pause translation in a manner similar to ER signal sequences. We have previously found that downstream translational slowing is important for mitochondrial mRNA targeting (Tsuboi et al 2020, Arceo et al 2022), but we believe that to be distinct to what the Reviewer #2 is addressing.

Figures 3-5. Microscopy. The false green color images in Figure 3B do not show up well. They may be better shown in grayscale, with only the multiple overlays in color.

Response: False color for fluorescent microscopy images are widely used because they help to visualize the results to the readers and also facilitate the interpretation of multiple overlays. The use of false color is also suggested by Reviewer #4.

Figure 3C should show the data spread for all 150 cells and normalise differently as discussed above for westerns. I do not believe that all 150 WT cells have exactly the same GFP intensity, which is what the present plot claims.

Response: As answered to point 3 made by this Reviewer, now all figures, including Fig. 3C, are made with Graphpad and scatter plot with all individual points plotted, additionally to showing the mean, SD and statistical analysis. Results correspond to three independent experiments and show a statistically significant difference in Pdr5-GFP intensity signal between wild-type and tif51A-1 mutant. Figure legend has been corrected accordingly.

For panels 3D-F image quantification should be shown so that the variation across a population is clear. Eg in violin plots, or showing every point. It should be clear what proportion of cells have GFP aggregates and what the variation in number of granules is.

Response: The quantification of cytoplasmic Yta12 aggregates is now included in Fig.3E, which shows significant differences between the tif51A-1 mutant and the wild-type strain. Results show the individual values from three independent experiments with a minimum of 150 cells counted. We used a bar graph in which the values (% of cells with 0, 1, 2 or 3 aggregates) for each independent experiment are shown together with the mean, SD and statistical analysis. Figure legend has been corrected accordingly. This information also responds to the comments made by Reviewer #1.

Figure 4H has no error bars.

Response: New Fig.4H now shows the individual values of each of the three independent replicates, mean and error bars (SD). Figure legend has been corrected accordingly.

Figure 5C normalises 2 WTs to 1 as in Figure 3C. Both would be better as violin plots.

Response: Results in Fig. 5C are now shown using Graphpad and scatter plot in which all individual values are plotted (not normalized wild-type to 1), and also mean, SD and statistical significance. Results correspond to three independent replicates with the fluorescence intensity measured in more than 150 cells.

Figure 5D/E shows 37{degree sign}C data only. Do tif51A-1 cells have aggregates at 25{degree sign}C?There are no error bars in Figure 5E or any indication of how many cells/replicates were quantified.

Response: Figures 5D and 5E only show data at 37ºC since there are no Tim50-GFP aggregates, nor aggregates of other mitochondrial proteins, in tif51A-1 mutants at 25ºC, as shown in Fig. S3C-F and Fig. S5C.

New Fig. 5E shows individual values from each of the three independent experiments, mean, SD and statistical significance. Results correspond to the measurement of Tim50 protein aggregates in more than 150 cells. Figure legend has been corrected accordingly.

There are no sizing bars on any of the micrographs.

Response: Now, all sets of microscopy figures contain a size bar and this is indicated in the corresponding Figure legend.

The methods states that all quantification was done using ImageJ, but there is no detail given about how this was done. There are lots of ways to use ImageJ.

Response: A detailed description of the quantifications made using ImageJ is now included in the Materials and Methods section (“Fluorescent microscopy and analysis” subsection).

Figure 4. Luciferase assay. It is clear that there are differences in Tim50 vs Tim50∆7pro signal over time from the primary plots. It is not clear why the quantification plots on the right are from 2 selected time points. It is more typical to calculate the rate of increase in RLU per min in the linear portion of the plot, for these examples it would be approximately 30-40 mins.

Response: As luciferase mRNA level is also increasing with time, the total amount of luciferase protein will increase exponentially. At some point mRNA levels will reach a steady state and for a brief period there could be a linear portion of RLU increase, but that will be different for each condition and reporter as ribosome quality control can have a direct impact on mRNA half-life. We have instead chosen two time points to show that statistical differences in Tim50 protein expression upon eIF5A depletion are not dependent on the time point chosen. We have also included the full data plots for readers to view the raw data.

Figure 4F. The text on p6 states Fig 4F is evidence of RQC induction. This is an overstatement. There are no data presented relating to RQC.

Response: Ribosome-associated quality control (RQC) is a mechanism by which elongation-stalled ribosomes are sensed in the cell, and then removed from the stall site by ribosomal subunit dissociation. This is the definition of RQC. With high levels of RQC this will cause a drop in ribosome density downstream of the stall site because of ribosome removal. While we would agree that most studies do not show actual buildup of ribosomes at ribosome stalls, and removal after the stall, we do. Our ribosome profiling analysis shows in vivo distribution of ribosome density across the TIM50 mRNA in wild-type and upon eIF5A depletion. We show that in the eIF5A depletion the ribosome density is similar to wild-type for the first ~200 bp, then there is a buildup of ribosomes for ~300 bps up to the stretch of polyproline residues, indicative of slowed ribosome movement. This slowed ribosome movement is further supported by our translation duration measurements in Fig. 4E. Then the transcript is almost completely devoid of ribosomes after the stretch of proline residues, indicating the ribosomes are removed at the proline stretch. This combination of ribosome stalling (Fig. 4E,4F) and subsequent ribosome removal (Fig 4F) is the textbook definition of RQC, so we indicate this as evidence for RQC.

Figure 5G. It is not clear to this reviewer why the CYC1 reporter is impacted by Tim50∆pro at 25{degree sign}C. Can the authors comment?

Response: This is also not clear to us, however, no differences are seen with and without eIF5A depletion, supporting the interpretation that Cyc1 translation is not affected by eIF5A depletion when Tim50 protein levels are restored in the Tim50∆pro strain. However, in order to clarify this point, we propose, if it is considered necessary, to remake the Tim50∆pro CYC1 reporter strain.

Does ∆pro impact Tim50 function or is there possibly some other off target impact of integrating the reporter in this strain?

Response: As answered to Reviewer #1 in her/his point 1, the functionality of Tim50ΔPro is shown by the fact that wild-type cells carrying this Tim50 protein version as the only copy of Tim50 grew well in glycerol media, where Tim50 is essential for the mitochondrial function (Fig. 5A). However, we suspect that Tim50ΔPro is a bit less efficient protein since a double mutant tif51A-1 Tim50ΔPro shows even reduced growth than the single tif51A-1 mutant (Fig. 5A). We do not expect off target impact in this Tim50ΔPro strains, although we cannot exclude this 100%, as in any other yeast strain obtained by transformation.

Significance

Strengths and Limitations:

Strengths are that the study uses a wide range of molecular approaches to address the questions and that the results present a clear story.

Limitations are that the poly-proline residues identified in yeast Tim50 are not conserved through to humans, so the direct relevance to higher organisms is unclear. However there are many more poly-proline proteins in human genes than in yeast and there are rare genetic conditions affecting eIF5A and its hypusination

Advance. provides a clear link between dysregulation of eIF5A, Tim50 expression and wider impact on mitochondria.

Audience. Scientists interested in protein synthesis, mitochondrial biology and clinicians investigating rare human disorders of eIF5A and hypusination.

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

eIF5A is required to mediate efficient translation elongation of some amino-acid sequences like polyproline motifs, and eIF5A depletion was reported to impair mitochondrial respiration functions, decreasing mitochondrial protein levels. In this study, Barba-Aliaga et al. showed that eIF5A is important for the translation of the Pro-repeat containing protein, Tim50, an essential subunit of the TIM23 complex, the presequence translocase in the mitochondrial inner membrane. eIF5A ts mutants caused ribosome stalling of Tim50 mRNA on the mitochondrial surface at non-permissive temperature, and the removal of the Pro-repeat from Tim50 (Tim50-delta7Pro mutant) made its translation independent of eIF5A. However, the replacement of endogenous Tim50 with Tim50-delta7Pro did not recover the cell growth defects of eIF5A ts mutant on respiration medium at semi-permissive temperature, suggesting that Tim50 is not the only reason for the global mitochondrial defects caused by defective eIF5A.

(1) I am wondering why the authors mainly used the eIF5A ts mutant strains instead of the eIF5A degron strain since, for example, the decrease in the level of Tim50 was only marginal (Fig. EV4A).

Response: eIF5A is a very abundant protein and with high stability (SGD data: 273594 molecules/cell in YPD and 9.1 h protein half-life). We have used temperature-sensitive strains, tif51A-1, instead of eIF5A-degron because eIF5A is depleted much quicker in the first than the second system. As it can be seen in Schuller et al., Mol Cell. 2017;66(2):194-205.e5. doi: 10.1016/j.molcel.2017.03.003, with the eIF5A-degron system the addition of auxin was made in parallel to a transcriptional shut off using GAL promoter to express eIF5A-degron, changing the media from galactose to glucose and incubating the cells for 10 hours. With our approach using temperature-sensitive proteins, almost full depletion (without affecting viability, see Li et al., Genetics 2014; 197(4):1191-200 doi: 10.1534/genetics.114.166926) can be done after 4-6 h incubation at 37ºC or 4 h incubation at 41ºC (Fig. 1C and Fig. S1E, almost no signal is detected by western blotting). Therefore, we chose to use eIF5A depletion with temperature-sensitive yeast strains to achieve stronger protein depletion with shorter times and avoid secondary effects. In addition, the two eIF5A temperature-sensitive strains used in this study have been widely used by us and others (Pelechano and Alepuz, 2017; Zanelli and Valentini, 2005; Zanelli et al., 2006; Dias et al., 2008; Muñoz-Soriano et al., 2017; Rossi et al., 2014; Li et al., 2014; Xiao et al., 2024).

(2) To show that the compromised translation of Tim50 in the absence of functional eIF5A causes defects in the mitochondrial protein import by clogging the import channels, the authors should directly observe the accumulation of the precursor forms of several matrix-targeting proteins by immunoblotting. In this sense, the results in Fig. 1C for Hsp60 do not fit the interpretation of import channel clogging.

Response: We did not see precursor mitochondrial proteins by Western blot upon eIF5A depletion possibly because: 1) the mature protein form is more abundant and stable; 2) the precursor mito-protein appears in cytoplasmic aggregates and this may not be easily extracted during preparation of proteins for Western blot analysis. In the work by Weidberg and Amon, 2018, who described the mitoCPR response; Krämer et al., 2023, who described mitostores; and others (Wrobel et al., 2015; Boos et al., 2019) the authors use extreme over-expression of mitoproteins or mutations in essential proteins for mitochondrial biogenesis to induce clogging of translocases and accumulation of precursors in the cytosol. However, we are using and detecting proteins at their physiological levels, expressed under their native promoters, what may explain why we do not detect precursor mito-proteins. We are using what we believe to be a much more physiologically relevant system, where we use endogenous expression of mitochondrially imported proteins. Yet we see similar transcriptional induction of mitoCPR targets (CIS1, PDR5, PDR15) and mislocalization of mitochondrial proteins to Hsp104 marked aggregates (MitoStores).

(3) The authors speculated in the Discussion section that import defects caused by compromised translation of Tim50 could cause down-regulation of translation through prolonged mitochondrial stress. However, this lacks experimental evidence.

Response: We do see that depletion of eIF5A causes import defects through Tim50 and correlates with the down-regulation of translation of mRNAs encoding mitoproteins as shown in Fig. 2C and Fig. S2. In these figures it can be seen that mito-mRNAs move from heavier to lighter polysomal fractions upon eIF5A depletion, indicating that less ribosomes are bound to these mRNAs. Importantly, synthesis of Cyc1 and Cox5A mitochondrial proteins is recovered when TIM50 gene is replaced by an eIF5A-translation independent TIM50ΔPro gene, arguing in favor of a translation defect caused by eIF5A depletion through the collapse of import systems produced by the ribosome stalling in TIM50 mRNA.

As discussed by Reviewer #2 and in our answers to his/her points 5 and 6, the reduction in the number of ribosomes bound to mito-mRNAs upon eIF5A depletion may be a consequence of the stall of ribosomes after the mRNA 5’ coding region encoding the MTS. This discussion has now been introduced in the Discussion section. This information also responds to the comments made by Reviewer #2.

(4) The authors stated that human Tim50 does not have Pro-repeat motif, but how about other organisms (like other fungi species)? Is the present observation specific only to S. cerevisiae?

Response: We have now included a sequence alignment of the Tim50 protein sequences of different yeast species (Saccharomyces cerevisiae, Candida albicans, Candida glabrata, Candida lipolytica, Schizzosaccharomyces pombe, Schizzosaccharomyces jamonicus), mouse and human (Fig. S4A). The resulting alignment shows that S. cerevisiae is the only organism presenting the seven consecutive proline residues. Still, C. albicans and C. glabrata conserve five consecutive prolines while C. lipolytica conserves five non-consecutive prolines. Furthermore, S. pombe and S. jamonicus, and mouse and human, conserve three and four non-consecutive prolines respectively. This means that the observations presented in this manuscript could be extended to other fungi species as well since most of the proline residues are conserved and are predicted to behave as eIF5A-dependent motifs for translation. Moreover, the described eIF5A-dependent tripeptide motif PDP is found in humans, mice and S. pombe at the Tim50 region where we found the PPP motif inducing ribosome stalling in S. cerevisiae (Fig S4A). This may confer eIF5A-dependent ribosome stall since as we showed in our previous ribosome footprinting (Pelechano et al., 2017), this PDP motif causes a similar high ribosome stall as the PPP motif. This discussion has now been introduced in the Results and Discussion sections.

(5) Two references in the text are marked with "?", which should be corrected.

Response: We thank you the Reviewer #3 for noticing this, references have been corrected in the text.

__Reviewer #3 (Significance (Required)): __

The essence of this work, the role of eIF5A in the efficient translation of Pro-repeat containing Tim50 (Figs. 4 and 5), is important and worth publication. However, the results of the effects of defective eIF5A on the levels and localization of mitochondrial proteins (Figs.1-3) can be even deleted to make clear the point of this work.

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

The manuscript submitted by Barba-Aliaga et al. aims to understand on the molecular level how eIF5A influences mitochondrial function. elF5A promotes translation elongation at stretches prone to translational stalling like e.g. polyproline sequence. The finding that eIF5a influences mitochondrial function has been previously reported by the same group and by others. In this context, it was suggested that eIF5a promotes translation of N-terminal mitochondrial targeting signals. Here, the authors propose an alternative mechanism and suggest that "eIF5a directly controls mitochondrial protein import through alleviation of ribosome stalling along TIM50 mRNA." Using luciferase reporter assay, the authors indeed convincingly show that the speed of Tim50 translation is dependent on the presence of functional TIF51A, the major eIF5a in yeast, and that this dependence comes from the presence of the polyproline stretch in Tim50. The rest of the manuscript is unfortunately less clear and it is very hard, if not impossible, to sort out direct from secondary effects and compensations. The authors use proteomics, biochemical methods, RNAseq and fluorescence microscopy to analyze the temperature sensitive tif51A mutant but the conditions used in the manuscript are non-consistent between various experiments presented, in respect to the medium, temperature, preculture condition and the length of treatment used.

Response: We do not agree with this Reviewer #4 appreciation. We used different molecular approaches to investigate different questions. Indeed, this is one of the Strengths that is highlighted by Reviewer 2 as it reads above: “Strengths are that the study uses a wide range of molecular approaches to address the questions and that the results present a clear story.” All the experiments presented in the manuscript, apart from proteomics analysis (Fig. 1), have been performed in the same conditions respect to the medium (SGal), temperature (25ºC/37ºC), preculture condition (SGal, 25ºC) and length of treatment used (4 h of depletion at 37ºC). This is already clearly specified in every Figure legend along the whole manuscript and also in the Materials and Methods section. In addition, individual values from each replicate, mean, standard deviation and statistical tests are shown for every Figure in the manuscript. Therefore, we do believe that conditions are consistent between experiments and conclusions are made based on different experiments and different scientific approaches.

We agree with Reviewer #4 in that depletion of eIF5A protein in the temperature sensitive tif51A-1 mutant was done in the proteomic at 41°C for 4 h, whereas in the rest of experiments depletion is made at 37°C for 4 h. As answered to Reviewer #2 (see answer to point 2), stronger depletion conditions were used to get clear proteomic results, and in order to compare both temperatures we have added now some controls showing eIF5A depletion and growth of tif51A-1 mutant at 41°C and 37°C; importantly, we also show the reduction in mito-protein levels upon eIF5A depletion at 37°C (Fig. S1B and E).

In some cases, the genetic background of the yeast strains and plasmids used are also unclear (e.g. pYES2-pGAL-FLAG-TIM50-GFP-URA3 - based on the provided description, TIM50 was inserted between FLAG and GFP tags; if so, mitochondrial targeting signal of Tim50 would be masked making its import into mitochondria impossible).

Response: We do not agree with this appreciation. The genetic background of the yeast strains is always the same along the whole manuscript (BY4741 background) and is clearly specified in Table S2. In this line, all the information regarding the plasmids used can be found at Table S3 and plasmids construction is extensively detailed in the Materials and Methods section (“Yeast strains, plasmids, and growth conditions” subsection).

Regarding the pYES2-pGAL-FLAG-TIM50-GFP-URA3 plasmid and as already mentioned in the text, we only used this plasmid to analyze by western blotting the protein synthesis of Tim50 independently of its subcellular localization. Our results (Fig. S4C) confirm that the synthesis defect of this Tim50 version upon eIF5A depletion is only due to the presence of the polyproline region. Importantly, we did not make any conclusion regarding import defects or protein localization based on these results.

I have no doubt that upon exposure of tif51A cells to 41{degree sign}C for 4h cells initiate a number of cellular responses including mitoCPR and formation of MitoStores, however, I don´t think that the authors convincingly show that these are initiated by reduced levels of Tim50 - on the contrary, the authors show that levels of Tim50 are actually not significantly changed. This can hardly be reconciled with the model proposed. In addition, should the effect of Tif51A on mitochondria primarily be due to its effect on Tim50, then Tim50deltaPro should rescue the phenotype of tif51a mutant but it didn´t; if anything, it made it worse (see Fig 5A - the double mutant grows worse than the single ones). Furthermore, expression of Cyc1 luciferase reporter is reduced in Tim50deltaPro strain even at permissive temperature, Figure 5G. Since cytochrome c is not a substrate of the presequence pathway this again points to the secondary effects that are being observed.

Response: We believe that our main results, summarized next and all performed at 37°C, do show that translation defects in TIM50 mRNA are the cause of the mitoCPR induction and formation of MitoStores. First, Tim50 protein levels are significantly reduced upon eIF5A depletion, as shown in Fig. S4A and S4B. Although being statistically significant, we agree that the reduction in Tim50 protein level is quantitatively low. This can be explained by the high stability of Tim50 protein, with a half-life of approximately 9.6 h (Christiano et al, 2014), which makes it more difficult to measure large differences in new protein synthesis. This is why we additionally used an accurate and quantitative test for showing the eIF5A-dependency for TIM50 mRNA translation: the fusion of the TIM50 DNA sequence to a TetO7-inducible nLuc reporter, which allows to monitor the appearance of new Tim50 protein and to estimate the translation elongation rate (Fig.4C-E). The ribosome stalling at TIM50 mRNA provoked by eIF5A depletion, where this mRNA is located at the mitochondrial surface to promote the import of nascent Tim50 protein during translation (Fig. S5B), may cause by itself the clogging of the protein import system even though yields only a slight reduction in total Tim50 cellular protein. Second, as Reviewer #4 pointed with our model, Tim50deltaPro should rescue the phenotype of tif51A-1 mutant and it does it: no mitoCPR induction and no mito-protein cytoplasmic aggregation are observed (Fig. 5D-F). Moreover, no differences in Cyc1- and Cox5a-nanoLuc synthesis are observed in the tif51A-1 Tim50ΔPro strain between depletion and not depletion conditions (Fig. 5E). These results strongly suggest that the mitochondrial protein import defects (and consequently the mitoCPR induction and mito-protein cytoplasmic aggregation) caused by eIF5A depletion are a consequence of ribosome stalling during TIM50 mRNA translation. However, Reviewer #4 is right in that mitochondrial respiration and growth in glycerol are not restored in the tif51A-1 Tim50ΔPro strain, even though Tim50 protein levels have been restored under eIF5A depletion conditions. As we discuss in the manuscript, we expect that there are additional mitochondrial proteins as targets of eIF5A, such as Yta12 and/or others. We have added further data pointing to ribosome stalling and RQC for other cotranslationally inserted mitochondrial proteins (Table S6). Accordingly, this has also been included in the Discussion section. However, the identification and study of these other mitochondrial targets goes beyond the aim of our current study.

Minor comments

1. Page 1, mitochondrial proteins cross do not the intermembrane space through Tom40 but rather the outer membrane Response: We think the Reviewer #4 misunderstood the sentence because we are saying exactly what he/she states: mitoproteins cross the outer membrane to the intermembrane space through Tom40. Thus our sentence is:

“Usually, mitoproteins contact the central receptor Tom20 and cross to the intermembrane space (IMS) through Tom40, the β-barrel pore-forming subunit.”

Therefore, we kept the sentence.

Page 4, ATP1 is present in the matrix and not the inner membrane

Response: This has been corrected. We thank the Reviewer for pointing this.

The citations are missing at several places - they are left as "?"

Response: References have been corrected in the text.

It would be nice if microscopy images were colored in magenta and cyan, rather than red and green, to make them accessible to a wider audience.

Response: Green and red colors for fluorescent microscopy images are widely used in high-impact journals, especially when showing mitochondrial proteins and mitochondrial marker Su9-mCherry (Hughes et al., 2016, eLife, doi: 10.7554/eLife.13943; Kakimoto et al., 2018, Scientific Reports, doi: 10.1038/s41598-018-24466-0; Kreimendahl et al, 2020, BMC Biology, doi: 10.1186/s12915-020-00888-z). However, if the Reviewers think this is essential for publication, microscopy images can be colored in magenta and cyan instead.

Formally speaking, Tim50 is not per se a translocase, it is either a component of the translocase or, more precisely, a receptor of the translocase. Similarly, Tom20 and Tom70 are not membrane transporters but rather receptors of the TOM complex.

Response: We have changed the title and text to be more precise in the description of the components of the mitochondrial import systems as suggested by Reviewer #4.

Reviewer #4 (Significance (Required)):

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This is a potentially interesting story, however, the conditions used for the analysis of the temperature sensitive mutants were either too harsh or these mutants are in general impossible to control, making the manuscript, in my opinion, unfortunately too premature for publication.

Response: We do not agree with the Reviewer #4 opinion, all experiments were done at 37ºC except the proteomic analysis that it is also confirmed further for Tim50 and Por1 proteins at 37ºC. We want to stress that we show all experiments with at least three biological replicates, individual values for each measurement are included now in the graphics as recommended by Reviewer #2, and the mean, SD and statistical tests are included. We make conclusions based in statistical significant differences along the manuscript. The temperature-sensitive yeast mutants used show reproducible analysis, they behave as expected in the controlled conditions used and they have been widely used in our lab and others (Pelechano and Alepuz, 2017; Zanelli and Valentini, 2005; Zanelli et al., 2006; Dias et al., 2008; Muñoz-Soriano et al., 2017; Rossi et al., 2014; Li et al., 2014; Xiao et al., 2024).

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Referee #4

Evidence, reproducibility and clarity

The manuscript submitted by Barba-Aliaga et al. aims to understand on the molecular level how eIF5A influences mitochondrial function. elF5A promotes translation elongation at stretches prone to translational stalling like e.g. polyproline sequence. The finding that eIF5a influences mitochondrial function has been previously reported by the same group and by others. In this context, it was suggested that eIF5a promotes translation of N-terminal mitochondrial targeting signals. Here, the authors propose an alternative mechanism and suggest that "eIF5a directly controls mitochondrial protein import through alleviation of ribosome stalling along TIM50 mRNA." Using luciferase reporter assay, the authors indeed convincingly show that the speed of Tim50 translation is dependent on the presence of functional TIF51A, the major eIF5a in yeast, and that this dependence comes from the presence of the polyproline stretch in Tim50. The rest of the manuscript is unfortunately less clear and it is very hard, if not impossible, to sort out direct from secondary effects and compensations. The authors use proteomics, biochemical methods, RNAseq and fluorescence microscopy to analyze the temperature sensitive tif51A mutant but the conditions used in the manuscript are non-consistent between various experiments presented, in respect to the medium, temperature, preculture condition and the length of treatment used. In some cases, the genetic background of the yeast strains and plasmids used are also unclear (e.g. pYES2-pGAL-FLAG-TIM50-GFP-URA3 - based on the provided description, TIM50 was inserted between FLAG and GFP tags; if so, mitochondrial targeting signal of Tim50 would be masked making its import into mitochondria impossible). I have no doubt that upon exposure of tif51A cells to 41{degree sign}C for 4h cells initiate a number of cellular responses including mitoCPR and formation of MitoStores, however, I don´t think that the authors convincingly show that these are initiated by reduced levels of Tim50 - on the contrary, the authors show that levels of Tim50 are actually not significantly changed. This can hardly be reconciled with the model proposed. In addition, should the effect of Tif51A on mitochondria primarily be due to its effect on Tim50, then Tim50deltaPro should rescue the phenotype of tif51a mutant but it didn´t; if anything, it made it worse (see Fig 5A - the double mutant grows worse than the single ones). Furthermore, expression of Cyc1 luciferase reporter is reduced in Tim50deltaPro strain even at permissive temperature, Figure 5G. Since cytochrome c is not a substrate of the presequence pathway this again points to the secondary effects that are being observed.

Minor comments

1. Page 1, mitochondrial proteins cross do not the intermembrane space through Tom40 but rather the outer membrane
2. Page 4, ATP1 is present in the matrix and not the inner membrane
3. The citations are missing at several places - they are left as "?"
4. It would be nice if microscopy images were colored in magenta and cyan, rather than red and green, to make them accessible to a wider audience
5. Formally speaking, Tim50 is not per se a translocase, it is either a component of the translocase or, more precisely, a receptor of the translocase. Similarly, Tom20 and Tom70 are not membrane transporters but rather receptors of the TOM complex.

Significance

This is a potentially interesting story, however, the conditions used for the analysis of the temperature sensitive mutants were either too harsh or these mutants are in general impossible to control, making the manuscript, in my opinion, unfortunately too premature for publication.

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Referee #3

Evidence, reproducibility and clarity

eIF5A is required to mediate efficient translation elongation of some amino-acid sequences like polyproline motifs, and eIF5A depletion was reported to impair mitochondrial respiration functions, decreasing mitochondrial protein levels. In this study, Barba-Aliaga et al. showed that eIF5A is important for the translation of the Pro-repeat containing protein, Tim50, an essential subunit of the TIM23 complex, the presequence translocase in the mitochondrial inner membrane. eIF5A ts mutants caused ribosome stalling of Tim50 mRNA on the mitochondrial surface at non-permissive temperature, and the removal of the Pro-repeat from Tim50 (Tim50-delta7Pro mutant) made its translation independent of eIF5A. However, the replacement of endogenous Tim50 with Tim50-delta7Pro did not recover the cell growth defects of eIF5A ts mutant on respiration medium at semi-permissive temperature, suggesting that Tim50 is not the only reason for the global mitochondrial defects caused by defective eIF5A.

1. I am wondering why the authors mainly used the eIF5A ts mutant strains instead of the eIF5A degron strain since, for example, the decrease in the level of Tim50 was only marginal (Fig. EV4A).
2. To show that the compromised translation of Tim50 in the absence of functional eIF5A causes defects in the mitochondrial protein import by clogging the import channels, the authors should directly observe the accumulation of the precursor forms of several matrix-targeting proteins by immunoblotting. In this sense, the results in Fig. 1C for Hsp60 do not fit the interpretation of import channel clogging.
3. The authors speculated in the Discussion section that import defects caused by compromised translation of Tim50 could cause down-regulation of translation through prolonged mitochondrial stress. However, this lacks experimental evidence.
4. The authors stated that human Tim50 does not have Pro-repeat motif, but how about other organisms (like other fungi species)? Is the present observation specific only to S. cerevisiae?
5. Two references in the text are marked with "?", which should be corrected.

Significance

The essence of this work, the role of eIF5A in the efficient translation of Pro-repeat containing Tim50 (Figs. 4 and 5), is important and worth publication. However, the results of the effects of defective eIF5A on the levels and localization of mitochondrial proteins (Figs.1-3) can be even deleted to make clear the point of this work.

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Referee #2

Evidence, reproducibility and clarity

The authors report here novel findings concerning the role of eIF5A in mediating protein import to mitochondria in the model eukaryote Saccharomyces cerevisiae. It was previously known from structural and other studies that the translation factor eIF5A binds to the E-site of stalled ribosomes to help promote peptide bond formation. It was inferred by ribosome footprinting and reporter studies assessing the impact of eIF5A depletion that eIF5A is particularly needed to translate several specific amino acid motifs including polyproline stretches. However additional target sequences are known.

Here a proteomics approach reveals clear evidence that mitochondrially targeted proteins are impacted by temperature sensitive mutations in eIF5A that deplete the factor, including those without polyprolines. The authors then use a range of molecular and cell biology to focus on the role of mitochondrial signal sequences/mitochondrial protein import and the mitochondrial stress response, before highlighting a role for poly-prolines in Tim50, a major mitochondrial protein import factor. Consistent with the ribosome footprinting done previously it is shown that a stretch of 7 prolines limit its translation when eIF5A is depleted and studies shown here are consistent with the idea that this has wider consequences for mitochondrial protein import and hence translation/stability of other proteins. However improved Tim50 translation alone, by eliminating the poly-proline motif, is not sufficient to overcome all consequences of eIF5A depletion for mitochondrial protein import and for viability, suggesting a wider role.

In general the text flows nicely, this could be a study that explains why a large number of mitochondrially targeted proteins are impacted by depletion of eIF5A in yeast. As the poly Pro sequence in Tim50 is not conserved in higher eukaryotes it is unclear how this observation will scale to other systems, but it provides an example of how studies in a relatively simple system can trace wide-spread impact of the loss of one component of a central pathway-here protein synthesis to altered translation of a key component of another process-mitochondrial protein import. Given that eIF5A and its hypusine modifying enzymes are mutated in rare human disorders, it is likely there will be interest in this study.

However, while the conclusions may be justified, there are significant deficiencies in how the experiments have been analysed and presented in this version of the manuscript that impact every figure shown, coupled with deficiencies in the methods section that all need to be addressed. Thus, we have here the basis of what should be a very interesting paper here, but there is a lot of work to do to remedy perceived weaknesses. It may be that the overall conclusions are entirely sound and appropriate, but I suspect that performing the statistics in less biased ways may change some of the significant differences claimed. Some explanations concerning how data analyses were conducted and the reasons for specific analysis decisions being made would also improve the narrative. These points are expanded on below.

All the edits suggested here are aimed at improving the rigor of reporting in this study. Depending on how they are answered some may become major issues, or they could all be minor.

1 Figure 1 shows proteomic data for response to heat shock at 41{degree sign}C. In the text it is made clear that two different temperature sensitive missense alleles the 51A-1 and 51A-3 were analysed, but the single volcano plot in Figure 1A does not say whether it is reporting one of these experiments compared to WT (which one) or some other analysis (ie have data from the 2 mutants been amalgamated somehow?). I would assume only one, but which one, and why only one plot? How different is the other experiment? Why does the Figure title say the experiment is an eIF5A deletion when it is not this?

2 Why were the experiments shown in Figure 1 done at 41{degree sign}C when all other experiments are done at 37{degree sign}C? This experimental difference is ignored in the text and no comparison of the impact of 37 vs 41 is made anywhere in the manuscript. For example it would be straightforward to perform a comparison of eIF5A depletion (by western blot), polyribosome profiles, strain growth/inhibition at both temperatures.

3 Western blot quantification. In Figure 1D and E the authors present western blot quantification. However they have chosen to normalise every panel to the signal in lane 1. This means that there is no variation at all in that sample as every replicate is =1. This completely skews the statistical assumptions made (because there will be variation in that sample) and effectively invalidates all the statistics shown. An appropriate approach to use is to normalise the signal in each lane to the mean signal across all lanes in a single blot. That way if all are identical they remain at 1, but importantly variation across all samples is captured. This should be done to the loading controls as well before working out ratios or performing any statistical analyses. For this type of experiment it is more appropriate to use Anova than a T-test. This advice applies to every western data analysis figure in the whole manuscript and so all associated statistics need to be done again from the original quantification values. If T-test is justified then a correction for multiple hypothesis testing should be applied.

1. In all bar chart figures in addition to showing the mean and SD, each replicate value should be shown (eg as done in Fig 2C). Graphpad allows individual points to be plotted easily.

5 Figure 2. Polysome profiles. The impact of translation elongation stalls on global polysome profiles is complex, but a global run off is highly unlikely. Stalls later in the coding region would be anticipated to cause an increase in ribosome density as more ribosomes accumulate (like cars queueing held at a red light). However where a stall is early in a longer ORF, for example at a signal sequence, then there is less opportunity for ribosomes to join and so for those mRNAs moving to lighter points in the gradient may be observed. This may also cause knock on effects on AUG clearance and initiation which the authors appear to see as there may be an increased 60S peak in the traces shown. Are there differences in overall -low vs high polysomes, the traces shown suggest there may be? Discussion of these points is merited in the results section given the subsequent qPCR experiment.

1. Figure 2 qPCR. Using qPCR to analyse RNA levels across polysome gradients is tricky for multiple reasons including that the total RNA level varies across fractions that can impact recovery efficiencies following precipitation of gradient fractions. Often investigators use a spike in control to act as a normalising factor. Here it is completely unclear what analysis was done because details are not stated anywhere. How were primers optimized, was amplification efficiency determined? Or are they assumed to be 100%, which they will not be? A detailed description or reference to a study where that is written is needed.

It would be helpful to state how long CDS are for these mRNAs and where 2-3/2-8 cut off made is what for determining what is 'short' vs 'long' and the scientific basis for selecting 2-3 vs 2-8, why 8? Were M fractions also used in qPCR, they appear to be ignored in the analysis as currently presented?

Which transcripts studied here encode proteins with signal sequences? As Signal sequence pauses early in translation should impact ribosome loading this is potentially important here as discussed above.

1. Figures 3-5. Microscopy. The false green color images in Figure 3B do not show up well. They may be better shown in grayscale, with only the multiple overlays in color. Figure 3C should show the data spread for all 150 cells and normalise differently as discussed above for westerns. I do not believe that all 150 WT cells have exactly the same GFP intensity, which is what the present plot claims. For panels 3D-F image quantification should be shown so that the variation across a population is clear. Eg in violin plots, or showing every point. It should be clear what proportion of cells have GFP aggregates and what the variation in number of granules is. Figure 4H has no error bars. Figure 5C normalises 2 WTs to 1 as in Figure 3C. Both would be better as violin plots. Figure 5D/E shows 37{degree sign}C data only. Do tif51A-1 cells have aggregates at 25{degree sign}C? There are no error bars in Figure 5E or any indication of how many cells/replicates were quantified.

There are no sizing bars on any of the micrographs The methods states that all quantification was done using ImageJ, but there is no detail given about how this was done. There are lots of ways to use ImageJ.

1. Figure 4. Luciferase assay. It is clear that there are differences in Tim50 vs Tim50∆7pro signal over time from the primary plots. It is not clear why the quantification plots on the right are from 2 selected time points. It is more typical to calculate the rate of increase in RLU per min in the linear portion of the plot, for these examples it would be approximately 30-40 mins.

2. Figure 4F. The text on p6 states Fig 4F is evidence of RQC induction. This is an overstatement. There are no data presented relating to RQC.

3. Figure 5G. It is not clear to this reviewer why the CYC1 reporter is impacted by Tim50∆pro at 25{degree sign}C. Can the authors comment? Does ∆pro impact Tim50 function or is there possibly some other off target impact of integrating the reporter in this strain?

Significance

Strengths and Limitations:

Strengths are that the study uses a wide range of molecular approaches to address the questions and that the results present a clear story.

Limitations are that the poly-proline residues identified in yeast Tim50 are not conserved through to humans, so the direct relevance to higher organisms is unclear. However there are many more poly-proline proteins in human genes than in yeast and there are rare genetic conditions affecting eIF5A and its hypusination

Advance. provides a clear link between dysregulation of eIF5A, Tim50 expression and wider impact on mitochondria.

Audience.

Scientists interested in protein synthesis, mitochondrial biology and clinicians investigating rare human disorders of eIF5A and hypusination.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Barba-Aliaga and colleagues describe a potential function of eIF5A for the control of TIM50 translation. The authors showed that in temperature-sensitive mutants of eIF5A several mitochondrial proteins are decreased including OXPHOS subunits, proteins of the TCA cycle and some components of protein translocases. Some precursor proteins appear to localize into the cytosol. As consequent of mitochondrial dysfunction, the expression of some stress components is induced. The idea is that eIF5A ribosome-stalling of the proline-rich Tim50 of the TIM23 complex and thereby controls mitochondrial protein set-up.

The findings are potentially interesting. However, some control experiments are required to substantiate the findings.

1. To support their conclusion the authors should show whether Tim50 levels are affected in the eIF5A-ts mutants used. How are the levels of TOM and TIM23 subunits? Furthermore, how are the levels of the Tim50 variant that lack the proline residues? Is the stability or function of Tim50 affected by these mutations?
2. How specific is the effect of eIF5A on Tim50? Is there any other mitochondrial substrate of eIF5A? It is not so clear to the reviewer why the authors focused on Tim50.
3. Figure 1A: Which tif51A strain was used?
4. Figure 1C: The authors should show the steady state levels of some OXPHOS/TCA components to confirm the findings of Figure 1A.
5. The manuscript contains several quantifications. However, central information like number of repeats or whether a standard deviation or S.E.M. is depicted are missing.
6. Figure 3: The authors propose that precursor form aggregates outside mitochondria. To assess the data, a quantification should address in how many cells are protein aggregates.
7. Do the observed aggregated proteins interact with Hsp104?

Significance

The manuscript by Barba-Aliaga and colleagues describe a potential function of eIF5A for the control of TIM50 translation. The authors showed that in temperature-sensitive mutants of eIF5A several mitochondrial proteins are decreased including OXPHOS subunits, proteins of the TCA cycle and some components of protein translocases. Some precursor proteins appear to localize into the cytosol. As consequent of mitochondrial dysfunction, the expression of some stress components is induced. The idea is that eIF5A ribosome-stalling of the proline-rich Tim50 of the TIM23 complex and thereby controls mitochondrial protein set-up.

The findings are potentially interesting. However, some control experiments are required to substantiate the findings.

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Reply to the reviewers

__Below is our point-by-point reply to the reviewer's comments __

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

PNKP is one of critical end-processing enzymes for DNA damage repair, mainly base excision & single strand break repair, and double strand break repair to a certain extent. This protein has dual enzyme function: 3' phosphatase and 5' kinase to make DNA ends proper for ligation. It has been demonstrated that PTM of PNKP (e.g., S114, S126), particularly phosphorylation by either ATM or DNAPK, is important for PNKP function in DNA damage repair. The authors found a new phosphorylation site, T118, of PNKP which might be modified by CDK1 or 2 during S phase. This modification of phosphorylation is involved in maintenance and stability of the lagging strand, particularly Okazaki fragments. Loss of this phosphorylation could result in increased single strand gaps, accelerated speed of fork progression, and eventually genomic instability. And for this process, PNKP enzyme activity is not that important. And the authors concluded that PNKP T118 phosphorylation is important for lagging strand stability and DNA damage repair.

Major comments

In general, enzymes have protein interactions with its/their substrates. If PNKP is phosphorylated by either/both CDK1/2, the protein interaction between these would be expected. However, the authors did not provide any protein interactions in PNKP and CDKs. *Thank you for your suggestion. We will perform GFP-pulldown assays using cell extracts from HEK293 cells expressing GFP-WT-PNKP, GFP-T118A-PNKP. And then to confirm the interaction of PNKP and CDK1/2, we will blot with CDK1 and CDK2 antibodies. *

It is not clear how T118 phosphorylation is involved in DNA damage repair itself as the authors suggested. The data presenting the involvement of T118 phosphorylation in this mechanism are limited. This claim opens more questions than answers. CDK1/2 still phosphorylates T118 in this DNA damage repair process? What would happen to DNA damage repair in which PNKP involves outside of S phase in terms of T118 phosphorylation?

Thank you for your comment. We have investigated how T118 phosphorylation is important in DNA damage repair by several experiments. In figure S8, we tested SSB and DSB repair abilities of PNKP KO cells expressing PNKP T118A mutant, in which PNKP T118 phosphorylation has critical roles in both SSB and DSB repair pathways. Interestingly, the result of SSB repair assay (figure S8A & B) may indirectly indicate that T118 phosphorylation is important for SSB repair throughout cell cycle as these SSBs are instantly induced by IR exposure and recovered only for 30 mins that is presumably not enough time for cells to go through cell cycle. Along with the repair abilities, we also analyzed a recruitment kinetics/ability to DNA damage in PNKP T118A and T118D mutants using laser micro-irradiation assay in figure S9. This result indicates that the phosphorylation of PNKP at T118 is controlling its recruitment to at least laser-induced DNA damage sites. Moreover, we have analyzed recruitment of PNKP to a single-strand DNA gap structure, which mimics intermediates of some DNA repair pathways and incomplete Okazaki fragment maturation, using cell extracts from PNKP KO cells expressing PNKP T118A and T118D mutants and biochemical assay in figure 4H. This assay is much cleaner and shows that loss of T118 phosphorylation impairs PNKP recruitment to the ssDNA gap structure. We believe that these data sufficiently support our model that the phosphorylation of T118 on PNKP is involved in DNA repair in general. However, we agree with that we have not yet directly tested DNA repair ability of PNKP T118A in outside of S-phase. Therefore, in addition to these data, we will perform H2O2-induced SSB and IR-induced DSB repair assay using EdU (S phase) pulse labelling in PNKP KO cells expressing PNKP T118A mutant, then we will measure the ADP-ribose intensity and pH2AX foci in EdU negative cells (outside of S phase as the reviewer suggested).

Along the same line with #1/2 comments, the recruitment of PNKP to the damage sites is XRCC1 dependent. Is not clear whether PNKP recruitment to gaps on the lagging strand is XRCC1 independent or dependent. It might be interesting to examine (OPTIONAL)

*Thank you for an important suggestion. XRCC1 acts as a scaffold of PNKP and is required for recruitment of PNKP for canonical SSB repair, although we propose that PNKP is involved in two pathways in DNA replication: PARP1-XRCC1-dependent ssDNA gap filling pathway and Okazaki fragment maturation pathway working with FEN1. It is still important to address how XRCC1 is required for PNKP recruitment to the single-strand gaps on nascent DNA. Therefore, we will perform iPOND analysis in XRCC1 knock down + GFP-WT-PNKP expressed HEK293 cells. *

Minor comments

In results: 'Generation of PNKP knock out U2OS cell line' - In figure S2A; There are no data regarding diminishing the phosphorylation of g-H2AX.

Thank you for your suggestion. We will add pH2AX blot data in fig S2A (all reviewers requested).

• By showing data in figure S2B/C/D/E, the authors describe 'PNKP KO cells impaired the SSBs repair activity'. However, as the authors mentioned in this manuscript, PNKP could bind to either XRCC1 or XRCC4. Also for this experiment, IR had been applied, which induces DNA double strand breaks. Therefore, it is not certain that the authors' description is fully supported by these data presented. Perhaps, SSB inducing reagents should be used instead of IR.

In figure S2B/C/D/E, we used gamma-ray as IR source, which classified as low energy transfer irradiation. which mainly act as indirect effect to the DNA. It is estimated gamma-ray induce DNA damage as 60-80% SSBs and 20-40 % DSBs. We believe our results are reasonable. In addition to these results, we will perform poly-ADP-ribose assay with H2O2 treatment to more specifically assess SSBs repair activity.

• Is there any FACS analysis data to support the description of the last sentence 'especially the phosphorylation of PNKP T118, is required for S phase progression and proper cell proliferation'?

Thank you for your suggestion. We will add the FACS analysis data of cell cycle profiles in PNKP KO cells expressing GFP, GFP-PNKP WT, T118A.

In results: 'CDKs phosphorylate T118 of PNKP ~~~ replication forks'

• In figure 3A, Is there any change in total PNKP (both GFP-tagged & endogenous) level?

*Thank you for your suggestion. We agree with your comment. We will add the PNKP expression analysis in different cell cycle population in asynchronized and synchronized cells (G1, S, G2/M samples). *

In results: 'Phosphorylation of PNKP at T118 ~~~ between Okazaki fragments'

• In figure 4D, What happens in the ADP-ribose level, when T118D PNKP is expressed?

*Thank you for your suggestion. This is interesting question. We will perform ADP-ribosylation assay in PNKP KO cells and PNKP KO cells expressing PNKP WT and T118D, and add data of ADP-ribose levels in those cells. *

In results: 'PNKP is involved in postreplicative single-strand DNA gap-filling pathway'

• The description regarding data presented in figure 6 is not clear enough. These data might suggest that wildtype U2OS does not have SSB which is a substrate for S1 nuclease (except under FEN1i and PARPi treatment), whereas PNKP KO has SSB during both IdU and CIdU incorporation, so that S1 nuclease treatment dramatically reduces the speed of fork formation in PNKP KO cells. Also In figure 6B/C/D, adding an experimental group of PNKP KO with S1 nuclease + PARPi might help to understand the role of PNKP during replication better. Also these additional data could support the description in discussion 'Furthermore, PNKP is required for the PARP1-dependent single-strand gap-filling pathway ~~~ DNA gap structure'.

• *

*We agree with reviewer's comment and suggestion. Since this point is also raised by reviewer 3, we will add the rationale of the experiment and more detailed description about the results, which would substantially improve this manuscript. We will also revise our representation in text followed by the comment. In addition to revising the text, we will add experiment groups of PNKP KO with S1 nuclease with/without PARPi as the reviewer suggested. *

In results: 'Phosphorylation of PNKP at T118 is essential for genome stability'

• In figure S8C, Did you measure g-H2AX foci disappearance for later time point, such as 24 hrs after DNA damage? Is not clear whether non-phosphorylated PNKP at T118 inhibit DNA damage repair or make it slower? How does T114A-PNKP behave in this experimental condition? T114 is well known target of ATM/DNAPK for DDR & DSB repair.

Thank you for your suggestion. We agree with your point. It is very important to analyze whether T118A mutant shows delayed or total loss of DSB repair ability. We will add the measurement of pH2AX foci at 24 hrs after IR in PNKP KO cells expressing GFP, WT-PNKP, T118A-PNKP. Although the analysis of pS114 PNKP is previously reported (Segal-Raz et al., EMBO reports, 2011 and Zolner et al., Nucleic Acids Research, 2011), we will also perform pH2AX assay in PNKP KO cells expressing S114A-PNKP as a control.

The result shown in figure S9 should be described in the result section, not in the discussion section.

Thank you for your suggestion. This is a point also raised by Reviewer 3. Since we are going to re-consider the layout of the manuscript upon the planned revision (as reviewer 3 suggested), we will move these points to the appropriate result section from the discussion.

**Referees cross-commenting**

I could see a similar degree of positive tendency toward the manuscript. I agree with the comments and suggestions in additional experiments made by reviewers 2 and 3. Those suggestions will improve an impact of the manuscript in the DNA damage repair field.

Reviewer #1 (Significance (Required)):

Significance

The authors discovered new phosphorylation site (T118) of PNKP which is an important DNA repair protein. This modification seems to play a role in maintenance of the lagging strand stability in S phase. This discovery is something positive in DNA repair field to expand the canonical and non-canonical functions of DNA repair factors.

The data presented to support PNKP functions and T118 phosphorylation in S phase seem solid in general, yet it is not sure how much PNKP is critical in the Okazaki fragment maturation process which is known that several end processing enzymes (like FEN1, EXO1, DNA2 etc which leave clean DNA ends.) are involved.

These finding might draw good attentions from researchers interested broadly in cell cycle, DNA damage repair, replication, and possibly new tumor treatment.

My field and research interest: DNA damage response (including cell cycle arrest and programmed cell death), DNA damage repair (including BER, SSBR, DSBR)

Thank you very much for your positive comment. As you mentioned, there are several other end processing enzymes that seem to be involved in Okazaki fragment maturation, however, none of those enzymes is reported as a protein involved in the gap-filling pathway as well. Therefore, the role(s) of PNKP in DNA replication are very outstanding as PNKP could be involved in two separate pathways, Okazaki fragment maturation and a back-up gap-filling repair process. As you suggested, we will add several experiments such as iPOND experiments using XRCC1-depleted cells, analysis of DNA repair ability of PNKP T118A mutant throughout cell cycle and S1 nuclease DNA fiber assays in PNKP KO cells with/without PARP inhibitor treatment, to reveal how much PNKP is critical in the Okazaki fragment maturation. We believe that performing those experiments makes the conclusion and this manuscript more solid and convincing.

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

Polynucleotide kinase phosphatase (PNPK) participates in multiple DNA repair processes, where it acts on DNA breaks to generate 5'-phosphate and 3'-OH ends, facilitating the downstream activities of DNA ligases or polymerases.

This manuscript identifies a CDK-dependent phosphorylation site on threonine 118 in PNKP's linker region. The authors provide some convincing evidence that this modification is important to direct the activity of PNPK towards ssDNA gaps between Okazaki fragments during DNA replication. The authors monitored protein expression levels, enzymatic activity, the growth rate and replication fork speed, as well as the presence of ssDNA damage to make a comprehensive overview of the features of PNKP necessary for its function.

Overall, the conclusions are sufficiently supported by the results and this manuscript is relevant and of general interest to the DNA repair and genome stability fields. Some level of revision to the experimental data and text would help strengthen its message and conclusions.

Major points:

In an iPOND experiment the authors detect the wt PNKP and the T118 phosphorylated form at the forks and conclude that this phosphorylation promotes interaction with nascent DNA (Figure 3E). An informative sample to include here would have been the T118A mutant. Based on the model proposed, the prediction would be that it would not be associated with the forks, or at least, associated at reduced levels compared to the wt. *Thank you for your suggestion. We agree with your comment. We will add the iPOND analysis in PNKP KO cells expressing T118A mutant to confirm that pT118 is important for recruitment of PNKP at nascent DNA. *

The quality of the gels showing the phosphatase and kinase assays in Figure 5 could be improved to facilitate quantification of the results. The gel showing the phosphatase activity has a deformed band corresponding to K378A mutant. The gel showing the kinase activity seems to be hitting the detection limits, and the overall high background might influence the quantification of D171A mutant in the area of interest. The authors should provide a better quality of these gels, focusing on better separation (running them longer, eventually with a slightly increased electric current) and higher signal of the analyzed bands (longer incubation phosphatase/kinase prior to quenching or loading higher amount of DNA).

We agree with your suggestion. This phosphatase and kinase assay could be improved. We will perform this assay again followed by reviewer's suggestions.

The authors sometimes make statements like: "a slight increase, slightly increased, relatively high" without an evaluation of the statistical significance for the presented data. An example of such a statement is: "T118A mutant-expressing cells exhibited a marked delay in cell growth, which was not observed for S114A, although T122A, S126A, and S143A were slightly delayed," based on the figure 2E. A similar comment applies also to figures 4A, 5A, 5E. Whenever possible, the authors should include also an evaluation of the statistical significance in the statement.

Thank you for your suggestion. We will check manuscript and revise representation as reviewer's suggestion.

Minor revisions:

I could not find a gH2AX blot for figure S2A.

Thank you for your suggestion. We will add pH2AX blot data in fig S2A.

The authors established two PNKP-/- clones and supported it with sequencing and several functional observations However, the C-terminal antibody appears to detect lower-intensity bands (Figure 1A). Can authors comment on those bands?

Thank you for your comment. One possibility of this band is artificially recognized bands. To improve this problem, we will try electrophoresis for longer time to separate this band.

Why the S1 nuclease data on DNA fibers do not show the same level of epistasis with the Fen1i, as do those on ADP-ribosylation?

Because FEN1 dependent Okazaki fragment maturation and PARP1-XRCC1 dependent gap-filling pathway are different pathways, FEN1i and PARPi treatment resulted in an additive effect in S1 nuclease data in PNKP WT cells. To facilitate better understanding, we will add graphical scheme in figure 6 (a similar problem was raised by Reviewer 3 below) and revise the description of the result.

**Referees cross-commenting**

I agree with all the comments from the reviewers 1 and 3.

Reviewer #2 (Significance (Required)):

Significance:

The manuscript identifies a CDK phosphorylation site in a relevant DNA repair protein. The experiments on this part are elegant and convincing. It seems that this phosphorylation is important during DNA replication and there is some supporting evidence in this point, although not as robust, meaning that it is not clear whether this phosphorylation is controlling specifically the recruitment to Okazaki fragments, or a general role in DNA repair. Maybe if they see a reduced recruitment of the T118A mutant to the forks (iPOND experiment) this would further increase the impact.

This work will be relevant to the basic research, especially in the fields of DNA repair and DNA replication.

My expertise: DNA replication, genome stability, telomere biology.

Thank you very much for your positive comment. As you suggested, we will perform an iPOND assay using PNKP T118A mutant. In addition of the T118A iPOND assay, we will also analyze the DNA repair function of PNKP T118A mutant throughout cell cycle as reviewer 1 suggested. We believe that results of these experiments will pin down whether the phosphorylation of PNKP on T118 is controlling its recruitment to Okazaki fragments specifically or single-strand DNA gaps in general, and solidify the conclusion of the manuscript.

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

Tsukada and colleagues studied the role of PNKP phosphorylation in processing single-strand DNA gaps and its link to fork progression and processing of Okazaki fragments.

They generated two PNKP KO human clonal cell lines and described defects in cell growth, accumulation in S-phase, and faster fork progression. With some elegant experiments, they complement the KO cell lines with deletion and point mutants for PNKP, identifying a critical phosphorylation site (T118) in the linker regions, which is important for cell growth and DNA replication.

They show that phosphorylation of PNKP peaks in the mid-S phase. CDK1 and CDK2/ with Cyclin A2 are the two main CDK complexes responsible for this modification. With the IPOND experiment, the author shows that PNKP is recruited at nascent DNA during replication.

They described increased parylation activity in PNKP KO cells, and by using HU and emetin, they concluded that this increased activity depends on replication and synthesis of Okazaki fragments.

Interfering with Okazaki fragment maturation by FEN1 inhibition is epistatic with PNKP KO (and T118A) in influencing parylation activity in the S phase and fork progression. The authors try to understand by mutant complementation which of the two functions (Phosphatase vs Kinase) is important in processing OF, and they propose a primary role for the phosphatase activity of PNKP. They also show that T118 is important in controlling genome stability following different genotoxic stress. Finally, by coupling the measurement of fork progression with PARP/FEN1 inhibitors and S1 treatment, they propose a role of PNKP in the post-replicative repair of single-strand gaps due to unligated OF.

Here are my major points:

The authors use a poly ADP ribose deposition measurement to estimate SSB nick/gap formation. Even if PARP activity is strictly linked to SSB repair, ADP ribosylation does not directly estimate SSB/nick gap formation. In addition, in Figs S2A, B, and C, the authors use IR and PARG inhibition to measure poly-ADP ribosylation in WT and PNKP KO cells. IR produces both SSB and DSB. A better and cleaner experiment would be to directly measure SSB formation (with alkaline comet assay, for example) in combination with treatments that are known to mainly cause SSB (H2O2, or low doses of bleomycin). Thank you for your suggestion. The main purpose of this manuscript is to clarify the potential role of PNKP in DNA replication. Therefore, we generated PNKP KO human cells and figure S2 showed confirmation of function of established role of PNKP in SSBs and DSBs repair. In addition, previous our report published in EMBO Journal (Shimada et al., 2015), we showed SSBs and DSBs repair defect in PNKP KO MEF with comet assay (both alkaline and neutral) after IR and H2O2 treatment. In addition to those observations, we will also perform BrdU incorporation assay in PNKP WT and KO cells treated with H2O2. BrdU staining under an undenatured condition has now been commonly used and is a more direct method to detect ssDNA nick/gap formation. We believe that the importance of PNKP in SSB repair is sufficiently supported by all data such as previous comet assays in PNKP KO MEF cells and two SSB repair assays in human cells using ADP-ribose staining or BrdU incorporation, which will be provided in the revised manuscript.

The manuscript would benefit from substantially restructuring the figures' order and panels. Before starting the T118 part, the authors could create several figures to explain the main consequences of the loss of PNKP. A figure could be focused on DSB-driven genome instability (fig1 + fig S8 and S9). Then, a figure for the single-strand break and link to the S-phase. For example, by using data from Figure 6 and showing only WT vs PNKP KO +- Nuclease S1 (without FEN1 or PARP inhibitors), the authors could easily convince the readers that loss of PNKP leads to the accumulation of single-strand gaps. Only in the second part of the manuscript could they introduce all the T118 parts. Thank you for your suggestion. The layout of this manuscript makes reviewers feeling confusing. After performing all planned experiments, we will carefully re-consider the total layout of the revised manuscript.

I understand the use of a FEN1 inhibitor to link the PNKP KO phenotype to OF processing, but this drug does not either rescue or exacerbate any of the phenotypes described by the authors. It seems to have just an epistatic effect everywhere. So, what other conclusion can we have if not that PNKO has a similar effect to FEN1? I think that the presence of this inhibitor in many plots complicates the digestion of several figures a little bit. Maybe clustering the data in a different way (DMSO on one side FEN1i on the other) would help. Thank you for your suggestion. We agree that this data set is complicate. To facilitate better understanding, we will change organization of the data according to your suggestion and add graphical scheme in figure 6.

In terms of the other conclusion we can have from those experiments, the other conclusion is that PNKP might plays two important roles in DNA replication: Okazaki fragment maturation, which seems an epistatic effect with FEN1, and PARP1-XRCC1 dependent single-strand gap filling pathway, which is required for repairing single-strand gaps between Okazaki fragments when Okazaki fragment maturation pathway does not work properly (e.g., loss of FEN1 or PNKP). In figure 6D, we show that a double treatment of FEN1i and PARPi in PNKP WT cells with S1 nuclease treatment shows extensive amount of digested DNA fibers, although a single treatment of either FEN1i or PARPi in PNKP WT cells with S1 nuclease treatment leads to only limited amount of digested DNA fibers, which indicates that two pathways regulated by FEN1 or PARP are coordinately required for preventing eruption of ssDNA gaps in DNA replication. On the other hand, PNKP KO cells with S1 nuclease treatment cause extensive amount of digested DNA fibers even without FEN1i and PARP1i treatments, also it is not further increased by FEN1i and PARPi treatment. Those results indicate that PNKP itself is involved in two pathways mentioned above. Therefore, loss of PNKP has a similar phenotype with loss of FEN1 in terms of Okazaki fragment maturation, but also there is an additional effect in repairing ssDNA nicks/gaps, which is created in FEN1 loss condition, but FEN1 seems not dealing with it.

Fig S9 should be removed from the discussion. Additionally, the authors should consider whether they want to keep that piece of data in a manuscript that is already pretty dense. Why should we focus on additional linker residues and microirradiation data at the end of this manuscript? *Thank you for your suggestion. This is a point also raised by Reviewer 1. Since we are going to re-consider the layout of the manuscript upon the planned revision, we will move these points to the appropriate result section from the discussion. *

I suggest using a free AI writing assistant. I think this manuscript would substantially benefit from one. As a non-native English speaker, I personally use one of them and find it extremely useful. Thank you for your suggestion. Our manuscript was revised by a native speaker from an English correction company. However, for revised manuscript, we will discuss with native speakers as well as use a free AI writing assistant to improve the quality of the manuscript.

Minor points:

In Figure S1A, the author refers to P-H2AX, but I do not see this marker in the western blot. Thank you for your suggestion. We will add pH2AX blot data in fig S2A.

**Referees cross-commenting**

I agree with all comments from reviewer 1 and 2.

Reviewer #3 (Significance (Required)):

This is an interesting paper with generally solid data and proper statistical analysis. The figures are pretty straightforward. Unfortunately, the manuscript is dry, and the reader needs help to follow the logical order and the rationale of the experiments proposed. This is also complicated by the enormous amount of data the authors have generated. The authors should improve their narrative, explaining better why they are performing the experiment and not simply referring to a previous citation. Reordering panels and figures would help in this regard. Overall, with some new experiments, tone-downs over strong claims and a better explanation of the rationale behind experiments the authors could create a fascinating paper.

Thank you very much for your positive comment about the data/analysis and the logic behind the experiments provided in the manuscript. We agree with that a manner and a structure of the manuscript could be improved by reordering figures, cutting down some redundant experiments, adding better explanation of the rationale behind experiments, and toning-down some claims. With rewriting the manuscript as stated above and performing several additional experiments suggested by the reviewers, we believe that the revised manuscript will be more convincing and fascinating.

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

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

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Reviewer #1:

Minor comments

• Is there any difference (except for PARGi exposure time?!) between figure S2B/C and S2D/E? Both data show increased ADP ribose after IR. It seems redundancy. Also it is hard to imagine that there is absolutely no sign of ADP ribose after IR w/o PARGi treatment (figure S2D).

Figure S2B/C show spontaneous single strand DNA breaks (SSBs) in PNKP KO cells, on the other hand, figure 2S/E show ectopic SSBs induced by IR exposure in PNKP KO cells. We believe these data help for readers to understand the effect of endo or exo damage in PNKP KO cells. Poly-ADP ribosylations are immediately removed from SSB sites after repair as demonstrated previously (Tsukada, et al., PLoS One 2019, Kalasova et al., Nucleic Acids Research, 2020), although not zero (low level), it is very difficult to detect without PARGi treatment.

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Legend for figure S3 - typo!

Thank you for your suggestion about typo. The legend for figure S3 is corrected as "Protein expression of PNKP mutants in U2OS cells".

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• In figure S3A/B, it is quite interesting that the PNKP antibody used for this analysis can detect all truncated and alanine substituted PNKP proteins. It might be helpful to indicate for other researchers which antibody used (Novus; epitope - 57aa to 189 aa or Abcam; epitope not revealed).

In S3A/B, Novus PNKP antibody was used for all blots. We indicated this in the figure legend as "PNKP antibody (Novus: NBP1-87257) was used for comparing expression levels of endogenous and exogenous PNKP".

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In results: 'PNKP phosphorylation, especially of T118 ~~~ proliferation'

• In the fork progression experiment (figure 2C), is there any statistical difference between D2 and D3/4 expressing cells?

*Thank you for your suggestion. We performed statistical analysis as the reviewer suggested. Statistical analysis shows that there are no significant differences between D2 and D3/D4. Meanwhile, there are significant differences between WT and D3(P- What is the basis of the description 'Since the linker region of PNKP is considered to be involved in fork progression'? Any reference?

This sentence was considered based on the above sentences "Furthermore, D2 mutant-expressing cells also showed an increased speed of the replication fork compared to WT and D1 mutant-expressing cells, although D3 and D4 showed mildly high-speed fork progression.". The D2 mutant lacks a whole linker region, which shows increased speed of DNA fiber in figure 2C. Therefore, we originally explained as the sentence above. We have revised the sentence to "Since these results may indicate the linker region of PNKP is involved in proper fork progression".

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• In figure 3B: pS114-PNKP (also pS15-p53) is DNA damage inducible. In this experiment, was DNA damage introduced? Roscovitine could hinder DNA repair process, but not inducing DNA damage itself.

Thank you for your suggestion. DNA damage induction was not applied in this experiment. We agree that this panel makes confusing. We think that endogenously S114-PNKP (also S15-p53) might be phosphorylated slightly but not significant, although this is not the scope of this manuscript. This result showing that phosphorylated-T118 is reduced by Roscovitine treatment maybe redundant as we also have a result of in vitro phosphorylation assay using several combinations of CDKs and Cyclin proteins, which is a cleaner experiment to prove which CDK/Cyclin complex is directly controlling the T118 phosphorylation. Since the manuscript already contains enough amount of data to support the conclusion (as reviewer 3 also stated), we removed those blots result from the panel to avoid complicating the conclusion.

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In results: 'Phosphatase activity of PNKP is ~~~ of Okazaki fragments'

• In figure 5C, any statistical analysis between WT-PNKP KO vs D171A-PNKP KO or K378A-PNKP KO has been done?

Thank you for your comment. Statistical analysis shows P *

In discussion, 'In contrast, the T118A mutants showed the absence of both SSBs and DSBs repair (Fig. S7) : figure S7 does not indicate what the authors describe.

Thank you for pointing out this. This should refer to figure S8 instead of figure S7. We have corrected this error.

In addition, the same sentence in discussion: No evidence demonstrate that 'the absence of both SSBs and DSBs repair', and the following sentence is not clear.

*This is same point with above. We have corrected this mis-referencing and revised the sentence to "In contrast, the T118A mutants showed the impaired abilities of both SSBs and DSBs repair (Fig. S8).". We also revised the following sentence to "However, residual SSBs due to impaired SSB repair ability (e.g., in PARPi-treated cells and T118A cells) sometimes cause DNA replication-coupled DSBs formation in S phase, and the phenotype in DSB repair assay of the T118A mutant may be caused by an accumulated formation of DNA replication-coupled DSBs. Future works will be needed to distinguish whether the T118 phosphorylation directly regulate PNKP recruitment to DSBs as well as SSBs." for better explanation of the result. *

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In discussion, 'Because both CDK1/cyclin A2 and CDK2/cyclin A2 are involved in PNKP phosphorylation, cyclin A2 is likely important for these activities': It is not clear what this description intends? Is 'cyclin A2' important in what stance?

This description is coming from Fig3C observation. Since both CDK1 and CDK2 activities are cyclin A2 dependent, we speculated cyclin A2 is important for CDK1/CDK2 dependent PNKP T118 phosphorylation. We revised the description to "Since both CDK1/Cyclin A2 and CDK2/Cyclin A2 phosphorylate T118 of PNKP, we speculated that PNKP T118 is phosphorylated in S phase to G2 phase in CDK1/Cyclin A2- and CDK2/Cyclin A2-dependent manner (Fig. 3B and C)".

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In discussion, 'This may be explained by the fact that mutations in the phosphorylated residue in the linker region are embryonic lethal': any reference to support this embryonic lethality?

Thank you for your suggestion. We agree with that this sentence is overwriting. We revise the sentence to "This observation may indicate that mutations in the phosphorylated residue (T118) in the linker region are potentially embryonic lethal due to the importance of T118 in DNA replication, which is revealed in the present study.".

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Reviewer #2:

Minor comments

Sometimes there are incorrect references to the figures in the discussion (e.g. FigS9A, B, and C, are called out instead of E, F and G), a similar issue is found 4 lines below in the same page.

Thank you for pointing out these errors. We checked the references in the discussion and corrected to the appropriate references.

Based on the data in Figure 3A the authors suggest that pT118-PNKP follows Cyclin A2 levels, but this does not appear very clearly in the gel, especially for the last point. Even though the results are convincing, the authors should rephrase the conclusions of Figure 3A to reflect better the results.

Thank you for your suggestion. We agree that this phrase is overwriting. We revised the conclusion to "pT118-PNKP was detected in asynchronized cells but increased particularly in the S phase, similar to Cyclin A2 expression levels, although the reduction of pT118, possibly dephosphorylation of T118, seems not as robust as the reduction of the Cyclin A2 expression level at the 12 hours time point. However, this effect was very weak during mitosis, suggesting that T118 phosphorylation plays a specific role in the S phase.".

I did not find a reference to what seems to be a relevant work in this topic: PMID: 22171004

Thank you for your suggestion. We have added the ref (Coquelle et al., PNAS, 2011) in Introduction section.

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Reviewer #3:

Major comments

The authors should consider and discuss the potential role of PNKP KO outside of the S-phase. In Figure 4C, while it is clear that poly ADP ribosylation is higher in S-phase, the effects of PNKP KO and complementation by WT or T118A are equally present. This would be more immediate if comparison, fold change, and statistical significance calculation were done within the same cell cycle phase instead of between cell stages. This is also clear by IF in Figure 4B. How do the authors explain this? Thank you for your suggestion. We agree with reviewer's suggestion. We compared intensities of ADP-ribose between cell lines in same cell cycle rather than between different cell cycles in a same cell line and added the respective statistics in figure 4C. Also, we agree with that poly ADP-ribose intensity is changed outside of S phase between WT and T118A PNKP expressing PNKP KO cells. As shown in figure S8, PNKP pT118 is also involved in DNA repair. These results might reflect of PNKP function outside of S phase. We have added the sentence "Of note, PNKP−/−*cells and PNKP T118A cells showed markedly higher ADP-ribose intensity in outside the S phase as well, which indicate that PNKP and T118 may have an endogenous role to prevent SSBs formation in outside the S phase. Since FEN1 has been reported to function in R-loop processing, PNKP could also be involved in this process. Future studies of a role of PNKP in different cell cycle will be able to address this question." to discuss about the function of PNKP outside the S phase. We have added the ref (Cristini et al., Cell Reports, 2019, and Laverde et al., Genes, 2022). *

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In connection with the previous point, can the author provide the same quantification in Figure 4E also for G2/M and not only the S phase? This should give an estimate of the activity of FEN1 outside the S-phase. This is important because FEN1 has other functions apart from OF maturation, such as R loop processing (Cristini 2019; Laverde 2023) Thank you for your suggestion. Here attached is the data of ADP-ribose intensity in cells outside the S phase as you suggested. FEN1i treatment still induces increased ADP-ribose intensity in outside the S phase as well, although the difference between with/without FEN1i treatment is much smaller than that in S phase, indicating that FEN1 has other functions outside the S phase. This finding is very interesting. However, the function of FEN1 in outside the S phase is outside the scope of this manuscript. Therefore, we would like to not put this data in the manuscript to avoid complicating the conclusion (as reviewer 3 also suggested).

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Why does FEN1 inhibition induce a faster fork progression in Fig4 but not in Fig5 and Fig6? Yes, it does in figure 4 and figure 5. In PNKP WT cells, FEN1i-treated fibers (CldU) show an increased speed of forks compared to non-treated fibers (IdU). However, loss of PNKP and T118 phosphorylation themselves cause a faster fork progression even if without FEN1i treatment, therefore the difference of speeds of forks before/after FEN1i treatment in PNKP KO and T118A cells is disappeared as both fibers grow faster than intact fibers in normal cells. In regard to figure 6, as you mentioned in a latter comment about figure 6, the title of vertical axis of the graph showing CldU length should not be speeds of replication forks as those DNA fibers are potentially digested by S1 nuclease, which is modified in the revised manuscript. Even so, DNA fibers from FEN1i-treated cells (CldU) with S1 nuclease shows similar length with fibers from untreated cells with S1 nuclease, whereas FEN1 inhibitor treatment accelerates a speed of forks in general (figure 4 and figure 5, assays without S1 nuclease), indicating that FEN1i treatment induces remaining of some ssDNA nicks/gaps which are substrates of S1 nuclease.

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How do the authors explain the impaired DNA gap binding activity of the phospho-mimetic T118D? Thank you for your suggestion. We think that the appropriate timing of phosphorylation of PNKP T118 is important, while the phosphor-mimetic mutant T118D mimics consecutively phosphorylated situation that may result in incomplete complementation of PNKP function.

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I would like to see a representative fiber image from Fig 6. Additionally, in Figure 6, the author should not label the y-axis as CldU-fork speed. Nuclease S1 treatment destroys single-strand gaps (in vitro) and does not affect the fork speed (in vivo) Thank you for your suggestion. We have added a representative fiber image. We also agree with that CldU fork speed is not a right label of y-axis as CldU fibers are potentially digested by S1 nuclease. We changed the y-axis label to "CldU tract length [kb/min]" in figure 6.

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Figure 5E: both mutants (kinase vs phosphatase) increase polyADP ribose intensity, while the title of this figure only emphasizes the phosphatase activity. We agree with your comment. We have changed this subtitle to "Enzymatic activities of PNKP is important for the end-processing of Okazaki fragments".

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Minor comments

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The authors refer to Hoch Nature 2017 when referring to polyADP ribose IF + PARG inhibition. Should they not refer to Hanzlikova Mol Cell 2018?

Thank you for your suggestion. We have added the ref (Hanzlikova et al., Mol Cell 2018).

Statistical analysis should be performed on the cell cycle profile in Figure 1B * *

We performed statistical analysis to check whether there are significant differences of S phase population between WT and PNKP KO cells. There were significant differences between WT vs PNKP KO C1 (PThe authors should not refer to fork degradation or protection as a given fact without assessing it in these conditions. Thank you for your suggestion. We assume that this comment refers to the result section of figure 1 and figure 4. We have added a sentence "although future studies will be needed to investigate whether PNKP−/− cells has the fork protection phenotype" in the result section of figure 1. We have changed representation in the section according to the reviewer's suggestion in the result section of figure 4.*

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Referee #3

Evidence, reproducibility and clarity

Tsukada and colleagues studied the role of PNKP phosphorylation in processing single-strand DNA gaps and its link to fork progression and processing of Okazaki fragments.

They generated two PNKP KO human clonal cell lines and described defects in cell growth, accumulation in S-phase, and faster fork progression. With some elegant experiments, they complement the KO cell lines with deletion and point mutants for PNKP, identifying a critical phosphorylation site (T118) in the linker regions, which is important for cell growth and DNA replication.

They show that phosphorylation of PNKP peaks in the mid-S phase. CDK1 and CDK2/ with Cyclin A2 are the two main CDK complexes responsible for this modification. With the IPOND experiment, the author shows that PNKP is recruited at nascent DNA during replication.

They described increased parylation activity in PNKP KO cells, and by using HU and emetin, they concluded that this increased activity depends on replication and synthesis of Okazaki fragments.

Interfering with Okazaki fragment maturation by FEN1 inhibition is epistatic with PNKP KO (and T118A) in influencing parylation activity in the S phase and fork progression. The authors try to understand by mutant complementation which of the two functions (Phosphatase vs Kinase) is important in processing OF, and they propose a primary role for the phosphatase activity of PNKP. They also show that T118 is important in controlling genome stability following different genotoxic stress. Finally, by coupling the measurement of fork progression with PARP/FEN1 inhibitors and S1 treatment, they propose a role of PNKP in the post-replicative repair of single-strand gaps due to unligated OF.

Here are my major points:

• The authors use a poly ADP ribose deposition measurement to estimate SSB nick/gap formation. Even if PARP activity is strictly linked to SSB repair, ADP ribosylation does not directly estimate SSB/nick gap formation. In addition, in Figs S2A, B, and C, the authors use IR and PARG inhibition to measure poly-ADP ribosylation in WT and PNKP KO cells. IR produces both SSB and DSB. A better and cleaner experiment would be to directly measure SSB formation (with alkaline comet assay, for example) in combination with treatments that are known to mainly cause SSB (H2O2, or low doses of bleomycin).
• The manuscript would benefit from substantially restructuring the figures' order and panels. Before starting the T118 part, the authors could create several figures to explain the main consequences of the loss of PNKP. A figure could be focused on DSB-driven genome instability (fig1 + fig S8 and S9). Then, a figure for the single-strand break and link to the S-phase. For example, by using data from Figure 6 and showing only WT vs PNKP KO +- Nuclease S1 (without FEN1 or PARP inhibitors), the authors could easily convince the readers that loss of PNKP leads to the accumulation of single-strand gaps. Only in the second part of the manuscript could they introduce all the T118 parts.
• The authors should consider and discuss the potential role of PNKP KO outside of the S-phase. In Figure 4C, while it is clear that poly ADP ribosylation is higher in S-phase, the effects of PNKP KO and complementation by WT or T118A are equally present. This would be more immediate if comparison, fold change, and statistical significance calculation were done within the same cell cycle phase instead of between cell stages. This is also clear by IF in Figure 4B. How do the authors explain this?
• In connection with the previous point, can the author provide the same quantification in Figure 4E also for G2/M and not only the S phase? This should give an estimate of the activity of FEN1 outside the S-phase. This is important because FEN1 has other functions apart from OF maturation, such as R loop processing (Cristini 2019; Laverde 2023)
• I understand the use of a FEN1 inhibitor to link the PNKP KO phenotype to OF processing, but this drug does not either rescue or exacerbate any of the phenotypes described by the authors. It seems to have just an epistatic effect everywhere. So, what other conclusion can we have if not that PNKO has a similar effect to FEN1? I think that the presence of this inhibitor in many plots complicates the digestion of several figures a little bit. Maybe clustering the data in a different way (DMSO on one side FEN1i on the other) would help.
• Why does FEN1 inhibition induce a faster fork progression in Fig4 but not in Fig5 and Fig6?
• How do the authors explain the impaired DNA gap binding activity of the phospho-mimetic T118D?
• Fig S9 should be removed from the discussion. Additionally, the authors should consider whether they want to keep that piece of data in a manuscript that is already pretty dense. Why should we focus on additional linker residues and microirradiation data at the end of this manuscript?
• I would like to see a representative fiber image from Fig 6. Additionally, in Figure 6, the author should not label the y-axis as CldU-fork speed. Nuclease S1 treatment destroys single-strand gaps (in vitro) and does not affect the fork speed (in vivo)
• Figure 5E: both mutants (kinase vs phosphatase) increase polyADP ribose intensity, while the title of this figure only emphasizes the phosphatase activity.
• I suggest using a free AI writing assistant. I think this manuscript would substantially benefit from one. As a non-native English speaker, I personally use one of them and find it extremely useful.

Minor points:

• In Figure S1A, the author refers to P-H2AX, but I do not see this marker in the western blot.
• The authors refer to Hoch Nature 2017 when referring to polyADP ribose IF + PARG inhibition. Should they not refer to Hanzlikova Mol Cell 2018?
• Statistical analysis should be performed on the cell cycle profile in Figure 1B
• The authors should not refer to fork degradation or protection as a given fact without assessing it in these conditions.

Referees cross-commenting

I agree with all comments from reviewer 1 and 2.

Significance

This is an interesting paper with generally solid data and proper statistical analysis. The figures are pretty straightforward. Unfortunately, the manuscript is dry, and the reader needs help to follow the logical order and the rationale of the experiments proposed. This is also complicated by the enormous amount of data the authors have generated. The authors should improve their narrative, explaining better why they are performing the experiment and not simply referring to a previous citation. Reordering panels and figures would help in this regard. Overall, with some new experiments, tone-downs over strong claims and a better explanation of the rationale behind experiments the authors could create a fascinating paper.

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Referee #2

Evidence, reproducibility and clarity

Polynucleotide kinase phosphatase (PNPK) participates in multiple DNA repair processes, where it acts on DNA breaks to generate 5'-phosphate and 3'-OH ends, facilitating the downstream activities of DNA ligases or polymerases.

This manuscript identifies a CDK-dependent phosphorylation site on threonine 118 in PNKP's linker region. The authors provide some convincing evidence that this modification is important to direct the activity of PNPK towards ssDNA gaps between Okazaki fragments during DNA replication. The authors monitored protein expression levels, enzymatic activity, the growth rate and replication fork speed, as well as the presence of ssDNA damage to make a comprehensive overview of the features of PNKP necessary for its function.

Overall, the conclusions are sufficiently supported by the results and this manuscript is relevant and of general interest to the DNA repair and genome stability fields. Some level of revision to the experimental data and text would help strengthen its message and conclusions.

Major points:

1. In an iPOND experiment the authors detect the wt PNKP and the T118 phosphorylated form at the forks and conclude that this phosphorylation promotes interaction with nascent DNA (Figure 3E). An informative sample to include here would have been the T118A mutant. Based on the model proposed, the prediction would be that it would not be associated with the forks, or at least, associated at reduced levels compared to the wt.
2. The quality of the gels showing the phosphatase and kinase assays in Figure 5 could be improved to facilitate quantification of the results. The gel showing the phosphatase activity has a deformed band corresponding to K378A mutant. The gel showing the kinase activity seems to be hitting the detection limits, and the overall high background might influence the quantification of D171A mutant in the area of interest. The authors should provide a better quality of these gels, focusing on better separation (running them longer, eventually with a slightly increased electric current) and higher signal of the analyzed bands (longer incubation phosphatase/kinase prior to quenching or loading higher amount of DNA).
3. The authors sometimes make statements like: "a slight increase, slightly increased, relatively high" without an evaluation of the statistical significance for the presented data. An example of such a statement is: "T118A mutant-expressing cells exhibited a marked delay in cell growth, which was not observed for S114A, although T122A, S126A, and S143A were slightly delayed," based on the figure 2E. A similar comment applies also to figures 4A, 5A, 5E. Whenever possible, the authors should include also an evaluation of the statistical significance in the statement.

Minor revisions:

1. I could not find a gH2AX blot for figure S2A.
2. Sometimes there are incorrect references to the figures in the discussion (e.g. FigS9A, B, and C, are called out instead of E, F and G), a similar issue is found 4 lines below in the same page.
3. The authors established two PNKP-/- clones and supported it with sequencing and several functional observations However, the C-terminal antibody appears to detect lower-intensity bands (Figure 1A). Can authors comment on those bands?
4. Based on the data in Figure 3A the authors suggest that pT118-PNKP follows Cyclin A2 levels, but this does not appear very clearly in the gel, especially for the last point. Even though the results are convincing, the authors should rephrase the conclusions of Figure 3A to reflect better the results.
5. Why the S1 nuclease data on DNA fibers do not show the same level of epistasis with the Fen1i, as do those on ADP-ribosylation?
6. I did not find a reference to what seems to be a relevant work in this topic: PMID: 22171004

Referees cross-commenting

I agree with all the comments from the reviewers 1 and 3.

Significance

The manuscript identifies a CDK phosphorylation site in a relevant DNA repair protein. The experiments on this part are elegant and convincing. It seems that this phosphorylation is important during DNA replication and there is some supporting evidence in this point, although not as robust, meaning that it is not clear whether this phosphorylation is controlling specifically the recruitment to Okazaki fragments, or a general role in DNA repair. Maybe if they see a reduced recruitment of the T118A mutant to the forks (iPOND experiment) this would further increase the impact.

This work will be relevant to the basic research, especially in the fields of DNA repair and DNA replication.

My expertise: DNA replication, genome stability, telomere biology.

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Referee #1

Evidence, reproducibility and clarity

Summary

PNKP is one of critical end-processing enzymes for DNA damage repair, mainly base excision & single strand break repair, and double strand break repair to a certain extent. This protein has dual enzyme function: 3' phosphatase and 5' kinase to make DNA ends proper for ligation. It has been demonstrated that PTM of PNKP (e.g., S114, S126), particularly phosphorylation by either ATM or DNAPK, is important for PNKP function in DNA damage repair. The authors found a new phosphorylation site, T118, of PNKP which might be modified by CDK1 or 2 during S phase. This modification of phosphorylation is involved in maintenance and stability of the lagging strand, particularly Okazaki fragments. Loss of this phosphorylation could result in increased single strand gaps, accelerated speed of fork progression, and eventually genomic instability. And for this process, PNKP enzyme activity is not that important. And the authors concluded that PNKP T118 phosphorylation is important for lagging strand stability and DNA damage repair.

Major comments

1. In general, enzymes have protein interactions with its/their substrates. If PNKP is phosphorylated by either/both CDK1/2, the protein interaction between these would be expected. However, the authors did not provide any protein interactions in PNKP and CDKs.
2. It is not clear how T118 phosphorylation is involved in DNA damage repair itself as the authors suggested. The data presenting the involvement of T118 phosphorylation in this mechanism are limited. This claim opens more questions than answers. CDK1/2 still phosphorylates T118 in this DNA damage repair process? What would happen to DNA damage repair in which PNKP involves outside of S phase in terms of T118 phosphorylation?
3. Along the same line with #1/2 comments, the recruitment of PNKP to the damage sites is XRCC1 dependent. Is not clear whether PNKP recruitment to gaps on the lagging strand is XRCC1 independent or dependent. It might be interesting to examine (OPTIONAL)

Minor comments

1. In results: 'Generation of PNKP knock out U2OS cell line'
   • In figure S2A; There are no data regarding diminishing the phosphorylation of g-H2AX.
   • Is there any difference (except for PARGi exposure time?!) between figure S2B/C and S2D/E? Both data show increased ADP ribose after IR. It seems redundancy. Also it is hard to imagine that there is absolutely no sign of ADP ribose after IR w/o PARGi treatment (figure S2D).
   • By showing data in figure S2B/C/D/E, the authors describe 'PNKP KO cells impaired the SSBs repair activity'. However, as the authors mentioned in this manuscript, PNKP could bind to either XRCC1 or XRCC4. Also for this experiment, IR had been applied, which induces DNA double strand breaks. Therefore, it is not certain that the authors' description is fully supported by these data presented. Perhaps, SSB inducing reagents should be used instead of IR.
2. Legend for figure S3 - typo!
   • In figure S3A/B, it is quite interesting that the PNKP antibody used for this analysis can detect all truncated and alanine substituted PNKP proteins. It might be helpful to indicate for other researchers which antibody used (Novus; epitope - 57aa to 189 aa or Abcam; epitope not revealed).
3. In results: 'PNKP phosphorylation, especially of T118 ~~~ proliferation'
   • In the fork progression experiment (figure 2C), is there any statistical difference between D2 and D3/4 expressing cells?
   • What is the basis of the description 'Since the linker region of PNKP is considered to be involved in fork progression'? Any reference?
   • Is there any FACS analysis data to support the description of the last sentence 'especially the phosphorylation of PNKP T118, is required for S phase progression and proper cell proliferation'?
4. In results: 'CDKs phosphorylate T118 of PNKP ~~~ replication forks'
   • In figure 3A, Is there any change in total PNKP (both GFP-tagged & endogenous) level?
   • In figure 3B: pS114-PNKP (also pS15-p53) is DNA damage inducible. In this experiment, was DNA damage introduced? Roscovitine could hinder DNA repair process, but not inducing DNA damage itself.
5. In results: 'Phosphorylation of PNKP at T118 ~~~ between Okazaki fragments'
   • In figure 4D, What happens in the ADP-ribose level, when T118D PNKP is expressed?
6. In results: 'Phosphatase activity of PNKP is ~~~ of Okazaki fragments'
   • In figure 5C, any statistical analysis between WT-PNKP KO vs D171A-PNKP KO or K378A-PNKP KO has been done?
7. In results: 'PNKP is involved in postreplicative single-strand DNA gap-filling pathway'
   • The description regarding data presented in figure 6 is not clear enough. These data might suggest that wildtype U2OS does not have SSB which is a substrate for S1 nuclease (except under FEN1i and PARPi treatment), whereas PNKP KO has SSB during both IdU and CIdU incorporation, so that S1 nuclease treatment dramatically reduces the speed of fork formation in PNKP KO cells. Also In figure 6B/C/D, adding an experimental group of PNKP KO with S1 nuclease + PARPi might help to understand the role of PNKP during replication better. Also these additional data could support the description in discussion 'Furthermore, PNKP is required for the PARP1-dependent single-strand gap-filling pathway ~~~ DNA gap structure'.
8. In results: 'Phosphorylation of PNKP at T118 is essential for genome stability'
   • In figure S8C, Did you measure g-H2AX foci disappearance for later time point, such as 24 hrs after DNA damage? Is not clear whether non-phosphorylated PNKP at T118 inhibit DNA damage repair or make it slower? How does T114A-PNKP behave in this experimental condition? T114 is well known target of ATM/DNAPK for DDR & DSB repair.
9. The result shown in figure S9 should be described in the result section, not in the discussion section.
10. In discussion, 'In contrast, the T118A mutants showed the absence of both SSBs and DSBs repair (Fig. S7) : figure S7 does not indicate what the authors describe.
11. In addition, the same sentence in discussion: No evidence demonstrate that 'the absence of both SSBs and DSBs repair', and the following sentence is not clear.
12. In discussion, 'Because both CDK1/cyclin A2 and CDK2/cyclin A2are involved in PNKP phosphorylation, cyclin A2 is likely important for these activities': It is not clear what this description intends? Is 'cyclin A2' important in what stance?
13. In discussion, 'This may be explained by the fact that mutations in the phosphorylated residue in the linker region are embryonic lethal': any reference to support this embryonic lethality?

Referees cross-commenting

I could see a similar degree of positive tendency toward the manuscript. I agree with the comments and suggestions in additional experiments made by reviewers 2 and 3. Those suggestions will improve an impact of the manuscript in the DNA damage repair field.

Significance

The authors discovered new phosphorylation site (T118) of PNKP which is an important DNA repair protein. This modification seems to play a role in maintenance of the lagging strand stability in S phase. This discovery is something positive in DNA repair field to expand the canonical and non-canonical functions of DNA repair factors.

The data presented to support PNKP functions and T118 phosphorylation in S phase seem solid in general, yet it is not sure how much PNKP is critical in the Okazaki fragment maturation process which is known that several end processing enzymes (like FEN1, EXO1, DNA2 etc which leave clean DNA ends.) are involved. These finding might draw good attentions from researchers interested broadly in cell cycle, DNA damage repair, replication, and possibly new tumor treatment.

My field and research interest: DNA damage response (including cell cycle arrest and programmed cell death), DNA damage repair (including BER, SSBR, DSBR)

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

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Reply to the reviewers

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

Summary: In this manuscript, the authors investigated the role of Erk signaling in the transition from naïve to formative pluripotency. They found that Erk activation eliminates Nanog to allow naïve state exit. However, when Nanog is knocked down in the absence of Erk activation, ESCs exit the naïve state, and enter an indetermined state, unable to proceed to the formative state. The authors further claimed that the failure to the formative state is due to lack of Oct4 expression. In conclusion, Erk signaling is required for the exit from the naïve state and the entry to the formative state.

Major comments: - Are the key conclusions convincing? Most of the key conclusions are convincing, except for the conclusion "ERK activity is required to maintain Oct4 expression in the naïve to formative pluripotency transition". The authors showed that Oct4 expression is diminished under the MEK(i)+siNanog condition, while Oct4 is expressed in N2B27+siNeg (Figure 4C). With these experimental setting, the conclusion that ERK activity is required to maintain Oct4 expression in the naïve to formative pluripotency transition, cannot be reached, because two variations, MEK(i) and siNanog, rather than one variation MEK(i), are there. The experiment should be designed as adding MEK(i) into N2B27+siNeg at various time points, to test whether MEK(i) is able to down-regulate Oct4 expression in the naïve to formative pluripotency transition.

We appreciate this point. We have now included data (figure 4C, 4E and S5B) to address this issue. As suggested, we performed exit experiments in MEK(i) only, and found that by 36hrs, a substantial proportion of cells have lost Oct4, unlike cells in N2B27 only. Down-regulation of Oct4 is later than in cells treated with MEK(i) + siNanog because of the delayed exit from the naïve state (in which Oct4 expression is independent of ERK). These data support the proposition that ERK activity is required to maintain Oct4 expression in the formative transition. We previously tried adding MEK(i) at various points in N2B27+siNeg conditions but the lack of synchrony made results impossible to interpret. As long as some Nanog positive cells remained, cells would re-activate the naïve network in the presence of MEK(i) and therefore maintain Oct4.

• 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. The suggested experiment was described above.

• 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. It should not cost too much in terms of funding and time.

• 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? Statistical analysis is lacking for Figure 3E and Figure 4.

We performed statistical analyses between key comparisons and have added details to the figures and captions.

Minor comments: - Specific experimental issues that are easily addressable. No.

• 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? No.

Reviewer #1 (Significance (Required)):

This work characterized the role of ERK signaling in the transition between naïve and formative pluripotency. The function of ERK in ESC self-renewal and differentiation has been well recognized. Thus, this work provides new discoveries, but no conceptual advances. It should be of interest to a specialized audience in the pluripotency field, which is my expertise.

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

Summary: In the present manuscript, Mulas and colleagues address the question how ERK signaling orchestrates the transition from naïve to formative pluripotency in mouse embryonic stem cells. Combining pharmacological MEK inhibition with siRNA knockdown of candidate transcription factors, they conclude that downregulation of Nanog is an immediate function of ERK signaling that underlies exit from the naïve state. Later on they show that ERK signaling has additional functions beyond downregulating Nanog that are required to make cells competent for formative pluripotency and lineage progression, such that Nanog knockdown cells enter a new indeterminate state in the absence of ERK signaling. Finally, they show that Oct4 is a central mediator of this second function of ERK signaling, since forced Oct4 expression rescues the expression of formative markers even in the presence of MEK inhibitors. They also present time-lapse imaging data of a Spry4- and a Nanog-reporter, based on which they propose that metachronous ERK activity is reflected in metachronous NANOG downregulation. The experiments dissecting the two different functions of ERK signaling in the pluripotency transition are well performed and provide some new interesting perspectives. Overall, the manuscript is well written. I have major concerns regarding the interpretation of the time-lapse imaging experiments (see major point 2 below) that unfortunately feature very prominently in the title of the manuscript.

Major points:

1. In lines 174 and 175, the authors write that "acute ERK activation ... [reduces] NANOG protein, which in turn dimishes Esrrb transcription". Although I am aware that this picture is supported by previous literature (e.g. PMID: 23040477), the author's data do not fully support this conclusion. In Fig. 1G for example, Esrrb is downregulated even though Nanog expression is maintained. This discrepancy needs to be discussed.

There is no real discrepancy because we are not claiming that Nanog is the only factor that regulates Esrrb. However, we recognise the potential for confusion. We have clarified our description of the results and included the statement: “Esrrb down-regulation can occur in part independently of Erk or Nanog.”. This does not invalidate the summary conclusion that “the proximal effect of acute ERK activation on the naïve transcription factor network is to reduce Nanog protein, which in turn diminishes Esrrb transcription.”

1. The imaging data and analysis presented in Fig. 2 do not support the conclusion that heterogeneous ERK dynamics underlies metachronous pluripotency exit. There are several problems with this section:

a. As far as I can see, the reporter line used in this study has not been previously used (at least there is no reference to a previous publication), and it has also not been properly validated in the present manuscript. One would for example like to know if the Spry4-FLuc allele encodes for a fusion protein, or whether it disrupts the Spry4 coding sequence. What is the half-life of the Spry4-Fluc protein? A proper description how the line has been generated, as well as an in-depth characterization are essential to evaluate the data.

We apologise for not providing full information. Both reporters have been previously published and validated. The Spry4 reporter is not a fusion protein. The Fluc is translated from an IRES. We have amended the text to include details of the construction of all the reporters, references and half-life measurements in the methods section that now reads: “Calibration cells (PGK-Nluc-Fluc - (Mandic et al., 2017) and cells carrying Spry4-Fluc transcriptional reporter (Phillips et al., 2019) and Nanog::Nluc fusion were routinely cultured in 2i/LIF as described above. The Spry4-FLuc construct contains a splice acceptor site, followed by an IRES and an Bsd/F2A/NLSluc cassette and has a half-life of 1.56hrs (Phillips et al., 2019). The Nanog:Nluc targeting construct was generating using the previously validated targeting construct for Sox2 (Strebinger et al., 2019) in which 5’ and 3’ homology arms flank a Nluc-loxP-P2A-Puro-sfGFP-loxP cassette. Integration of Nanog::Nluc was initially verified by GFP and Nluc expression, and finally by PCR following excision of the loxP cassette. Using cycloheximide treatment we determined that the reporter had a half-life of 3.02hrs.”

b. It is not clear that dynamic expression of a Spry4 reporter reflects dynamic ERK signaling. It has been shown that cumulative transcription from the Spry4 locus correlates with long-term ERK activity (e.g. PMID: 29964027), but short-term Spry4-FLuc dynamics could well be driven by other mechanisms, such as transcriptional bursting. Co-staining of ppERK and reporter expression in single cells would be required to address this issue.

This is a valid point of discussion. Comparing between reporter systems is difficult since the Spry4 reporter used in PMID: 29964027 is fluorescent protein based and is therefore dependent on the time of protein maturation (although very fast compared to other fluorescent proteins) and a half-life of 9hrs as reported by the authors. The bioluminescent reporter requires no maturation time and has a half-life of 1.65hrs (PMID: 28456689).

Below are our considerations for the choice of reporter and the interpretation of results:

1. We previously showed that during exit from the naïve state, at the bulk level, pERK activity and some pERK transcriptional targets show dynamic patterns of activity (PMID: 29895711). Therefore, a dynamic pattern of Spry4 expression is not unexpected.
2. We initially tested different means of measuring ERK activity more directly (ERK-KTR and EKAREV-NLS and EKAREV-NES) but the imaging frequency (

   c. Why is the Spry4-FLuc signal higher at the start of the recording (when cells come out of MEK inhibition and should not have transcribed the reporter) compared to times > 7.5 h, when continuous ERK signaling in N2B27 should drive reporter expression?

After media change, we typically allowed cells to equilibrate for 30min in the incubator before setting up the imaging. Therefore, there is a ~45min window in which we lack data. From experience (Nett*, Mulas* et al 2018), we know that pERK activity increases within 5-10min after MEK(i) withdrawal and that explains why Spry4-Fluc signal is high as soon as we start the recording. We have now included this clarification in the methods (line 392).

d. What is the evidence for temporally heterogeneous ERK activation? The authors only show one single trace in Fig. 2B, in which the Spry4-FLuc signal peaks right after release from 2i, as would be expected. Another study using a more direct ERK activity sensor (PMID: 31064783) indicated that this initial ERK activity peak after release from 2i is synchronous in all cells in a population. The authors would need to show several or all Spry4-FLuc traces from their experiment to demonstrate the opposite, otherwise one needs to assume synchronous ERK activation upon release from 2i in the author's experiments as well.

Following the reviewer’s suggestion, we now provide an additional supplementary figure with all the traces (Supporting Figure 1). This demonstrates asynchrony in the response. Moreover, as per the reviewer’s suggestion, we have now included immunostainings of the first wave of pERK response (In addition, Deathridge et al. included serum in all ESC culture conditions (according to their Methods) which creates a more complex signalling environment.

e. Why does the cross-correlation of the Spry-FLuc promoter activity (which should go up upon ERK signaling) with the NANOG-NLuc signal (which should go down upon ERK signaling) give positive values? Does this positive correlation reflect the transient nature of Spry4-FLuc expression, thus giving a positive value when Spry4-FLuc promoter activity decays? In this case, what is the meaning of the delay? Overall I found the explanation of this cross-correlation analysis very confusing. Given these problems, I recommend the authors to strongly tone down their conclusions or remove this section altogether, since addressing this multitude of problems might be out of scope for the present manuscript.

Cross-correlation explicitly includes an analysis of the changes in correlation when a lag (meaning a shift in time) is applied to one of the signals. Therefore, there is no “positive correlation” but rather “positive correlation with a given lag applied”. An example is cross-correlation between a sine wave and a cosine wave (which are going in opposite directions for half the points in any given period and so show a positive correlation with a time lag). In our case, if we time shift the Spry4 signal, it will cross-correlate with the Nanog signal. It is possible we are misunderstanding the point of confusion, but we have reviewed our analysis of the data and believe it to be sound. Moreover, in our opinion the findings represent an important component of our paper and add weight to the conclusions drawn.

However, we agree that the analysis could be better explained. We have substantially re-written the section with this aim. The main text now reads:

“We examined the relationship between Spry4 activation and Nanog protein downregulation. After smoothing to remove noise, we used a simple set of ordinary differential equations to calculate the Spry4 promoter activity for each Spry4-Fluc trace (Figure S2C, see methods for details). We created continuous traces by adding the measurements made from each cell end-to-end (Figure S2D). We then measured the cross-correlation between activity of the Spry4 promoter and Nanog protein level. As controls we randomised the Spry4 signal in two ways: first, we randomised the Spry4 signals to measure correlations between Spry4 promoter activity and Nanog downregulation that could be attributable to noise; second, we assigned random time shifts to the Spry4 traces recorded (schematic diagrams shown in Figure S2D). Cross-correlation for the real data is higher than for either of the controls, meaning that the measured Spry4 and Nanog signals are correlated above noise levels and there is a consistent time delay between the two signals. We repeated the analysis for individual traces and observed the same trend (Figure S2F-G, 2D-E). The average lag time is ~80min, indicating that activation of the Spry4 promoter precedes Nanog downregulation. We repeated the analysis for RSK(i) treated cells and observed a stronger correlation at the level of the combined dataset (Figure 2F) as well as in individual cells (Figure 2G, S2H). Interestingly, RSK(i) treatment, which leads to a more sustained peak of pERK1/2 activity (Figure S2B), decreased the average delay (lag) between Spry4promoter activation and Nanog downregulation to 20 min (Figure 2H, S2I). The fact that the lag is short, and not evident in all cells, suggests that Nanog downregulation might not require transcriptional activation.”

Overall we observe a significant cross-correlation between the rise in Spry-Fluc promoter activity (indicating active ERK-signalling) and the fall in Nanog-Nluc signal.

However, we agree that this is not the most decisive result in the study and have changed the title of the paper to “Erk signalling eliminates Nanog and maintains Oct4 to drive the formative pluripotency transition”.

1. In line 217 (section title), the authors write that "failure to transition is not due to genome-wide chromatin dysregulation". It is true that the changes upon MEK inhibition reported in this section are small, but there are some changes, and it is ultimately difficult to know which ones are essential. I suggest to rephrase this section title.

We have adjusted the section title.

1. The main finding of Fig. 4 - that Oct4 expression enables formative capacity - is very interesting. One problem throughout this figure is that the authors contrast the control case (N2B27/DMSO + siNeg) with a double perturbation (MEKi + siNanog), making it difficult to demonstrate whether it is the loss of Nanog or the loss of ERK signaling (or both) that results in loss of Oct4 expression. If I have missed something here please clarify.

We agree with this comment (also pointed out by the other reviewer). We have now included a new figure, showing that treatment with MEK(i) alone leads to loss of Oct4 expression after naïve state exit (updated figure 4E and S5B).

1. Can the authors speculate, or perhaps even experimentally explore, why Oct4 re-expression enables formative capacity? Oct4 positively regulates Fgf4 expression (PMID: 9814708), raising the possibility that the indeterminate state is caused by insufficient paracrine FGF4 signaling once cells have reached this indeterminate state. Alternatively, Oct4-mediated regulation of a broader set of lineage specifiers might be required to establish formative pluripotency. The authors could explore these possibilities by supplementing cultures with recombinant FGF ligands. While these experiments are not essential for to corroborate conclusions in the present manuscript, could allow the authors to follow up upon what I think is their most interesting finding, and thereby give the manuscript a lift.

The reviewer raises an interesting point of discussion. In our study transgene driven Oct4 expression was able to induce formative gene expression in MEK(i) conditions, which block FGF/ERK signalling (Figure 4F). Previous studies have shown that relocation of Oct4 to multiple gene loci is instrumental in the formative transition (PMID: 24905168 and PMID: 23271975) and it is known that Oct4 is an essential factor for formative stem cells (PMID: 33271069) and primed EpiSCs (PMID: 29915126).

Nonetheless we performed experiments to test whether addition of FGF could help rescue expression of formative genes after MEK(i) withdrawal (not shown). However, addition of FGF reduced neural differentiation in control cells and further reduced Sox1 expression in MEK(i)/siNanog treated cells (not shown). Moreover, we saw no significant upregulation of formative genes with addition of FGF (not shown). We decided not to include these results since the literature on the essential role of Oct4 throughout pluripotency is extensive.

Minor points: 6. Please explain in the methods how gates for identifying RGd2-positive and -negative cells in Fig. 1 B, E have been determined from the FACS plots in Fig. S1C/1B.

We have added a section in the methods to explain how this is done (Methods section “Flow Cytometry”), and we have now included a representative example in Figure S1C.

1. For the categorization of marker-positive and -negative cells in immunofluorescence images, the authors should explain in more detail according to which criterion a threshold was determined by ROC analysis. Which positive and negative controls were used in each case?

We have added the information to the methods section (Immunostaining and quantification).

1. Does a statistical test on the data in Fig. S1A,B reveal significant differences?

We have now performed appropriate statistical tests and have added them to both plots to show that there is indeed a significant difference.

1. Please give units on the x-axis in Fig. 2C?

Amended.

1. Fig. 3E: Consider re-arranging. It is not immediately clear that all five bar charts belong to this panel.

The experiments were carried out in parallel so we feel that the best way to present them is as currently shown.

1. There is a typo in Fig. S4A - mainteined

Amended.

1. Methods, lines 408 - 410: Please state units of the parameters used to estimate promoter activity.

Amended.

**Referee Cross-Commenting**

I agree with reviewer #1's assessment of significance and their reservation regarding the conclusion "ERK activity is required to maintain Oct4 expression in the naïve to formative pluripotency transition". The experiment that the reviewer suggests is reasonable and doable (see also my major point 4.). Even though reviewer #1 has not explicitly commented on the conclusions drawn from Fig. 2, I disagree with their assessment that these conclusions are convincing (see my major point 2.).

Reviewer #2 (Significance (Required)):

The control of pluripotency transitions by signaling mechanisms as well as transcription factor circuits have been mapped in quite some detail over the last decade. The main advance of this manuscript is that it looks at the interaction between these two levels and thereby provides some new and interesting links. These results will mainly be of interest to a large community of researchers working with pluripotent stem cells. To me, the most intriguing finding of the paper is the indeterminate cell state that the authors detect upon combined Nanog knockdown and MEK inhibition. To my knowledge, such a dead end of differentiation has not been reported before, at least not with pluripotent cells. This result could be a starting point for further investigation, and is of potential interest to a broader stem cell community.

Expertise: As a stem cell biologist I have the expertise to evaluate all parts of the paper.

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:

In the present manuscript, Mulas and colleagues address the question how ERK signaling orchestrates the transition from naïve to formative pluripotency in mouse embryonic stem cells. Combining pharmacological MEK inhibition with siRNA knockdown of candidate transcription factors, they conclude that downregulation of Nanog is an immediate function of ERK signaling that underlies exit from the naïve state. Later on they show that ERK signaling has additional functions beyond downregulating Nanog that are required to make cells competent for formative pluripotency and lineage progression, such that Nanog knockdown cells enter a new indeterminate state in the absence of ERK signaling. Finally, they show that Oct4 is a central mediator of this second function of ERK signaling, since forced Oct4 expression rescues the expression of formative markers even in the presence of MEK inhibitors. They also present time-lapse imaging data of a Spry4- and a Nanog-reporter, based on which they propose that metachronous ERK activity is reflected in metachronous NANOG downregulation.

The experiments dissecting the two different functions of ERK signaling in the pluripotency transition are well performed and provide some new interesting perspectives. Overall, the manuscript is well written. I have major concerns regarding the interpretation of the time-lapse imaging experiments (see major point 2 below) that unfortunately feature very prominently in the title of the manuscript.

Major points:

1. In lines 174 and 175, the authors write that "acute ERK activation ... [reduces] NANOG protein, which in turn dimishes Esrrb transcription". Although I am aware that this picture is supported by previous literature (e.g. PMID: 23040477), the author's data do not fully support this conclusion. In Fig. 1G for example, Esrrb is downregulated even though Nanog expression is maintained. This discrepancy needs to be discussed.
2. The imaging data and analysis presented in Fig. 2 do not support the conclusion that heterogeneous ERK dynamics underlies metachronous pluripotency exit. There are several problems with this section:
   • a. As far as I can see, the reporter line used in this study has not been previously used (at least there is no reference to a previous publication), and it has also not been properly validated in the present manuscript. One would for example like to know if the Spry4-FLuc allele encodes for a fusion protein, or whether it disrupts the Spry4 coding sequence. What is the half-life of the Spry4-Fluc protein? A proper description how the line has been generated, as well as an in-depth characterization are essential to evaluate the data.
   • b. It is not clear that dynamic expression of a Spry4 reporter reflects dynamic ERK signaling. It has been shown that cumulative transcription from the Spry4 locus correlates with long-term ERK activity (e.g. PMID: 29964027), but short-term Spry4-FLuc dynamics could well be driven by other mechanisms, such as transcriptional bursting. Co-staining of ppERK and reporter expression in single cells would be required to address this issue.
   • c. Why is the Spry4-FLuc signal higher at the start of the recording (when cells come out of MEK inhibition and should not have transcribed the reporter) compared to times > 7.5 h, when continuous ERK signaling in N2B27 should drive reporter expression?
   • d. What is the evidence for temporally heterogeneous ERK activation? The authors only show one single trace in Fig. 2B, in which the Spry4-FLuc signal peaks right after release from 2i, as would be expected. Another study using a more direct ERK activity sensor (PMID: 31064783) indicated that this initial ERK activity peak after release from 2i is synchronous in all cells in a population. The authors would need to show several or all Spry4-FLuc traces from their experiment to demonstrate the opposite, otherwise one needs to assume synchronous ERK activation upon release from 2i in the author's experiments as well.
   • e. Why does the cross-correlation of the Spry-FLuc promoter activity (which should go up upon ERK signaling) with the NANOG-NLuc signal (which should go down upon ERK signaling) give positive values? Does this positive correlation reflect the transient nature of Spry4-FLuc expression, thus giving a positive value when Spry4-FLuc promoter activity decays? In this case, what is the meaning of the delay? Overall I found the explanation of this cross-correlation analysis very confusing. Given these problems, I recommend the authors to strongly tone down their conclusions or remove this section altogether, since addressing this multitude of problems might be out of scope for the present manuscript.
3. In line 217 (section title), the authors write that "failure to transition is not due to genome-wide chromatin dysregulation". It is true that the changes upon MEK inhibition reported in this section are small, but there are some changes, and it is ultimately difficult to know which ones are essential. I suggest to rephrase this section title.
4. The main finding of Fig. 4 - that Oct4 expression enables formative capacity - is very interesting. One problem throughout this figure is that the authors contrast the control case (N2B27/DMSO + siNeg) with a double perturbation (MEKi + siNanog), making it difficult to demonstrate whether it is the loss of Nanog or the loss of ERK signaling (or both) that results in loss of Oct4 expression. If I have missed something here please clarify.
5. Can the authors speculate, or perhaps even experimentally explore, why Oct4 re-expression enables formative capacity? Oct4 positively regulates Fgf4 expression (PMID: 9814708), raising the possibility that the indeterminate state is caused by insufficient paracrine FGF4 signaling once cells have reached this indeterminate state. Alternatively, Oct4-mediated regulation of a broader set of lineage specifiers might be required to establish formative pluripotency. The authors could explore these possibilities by supplementing cultures with recombinant FGF ligands. While these experiments are not essential for to corroborate conclusions in the present manuscript, could allow the authors to follow up upon what I think is their most interesting finding, and thereby give the manuscript a lift.

Minor points:

1. Please explain in the methods how gates for identifying RGd2-positive and -negative cells in Fig. 1 B, E have been determined from the FACS plots in Fig. S1C/1B.
2. For the categorization of marker-positive and -negative cells in immunofluorescence images, the authors should explain in more detail according to which criterion a threshold was determined by ROC analysis. Which positive and negative controls were used in each case?
3. Does a statistical test on the data in Fig. S1A,B reveal significant differences?
4. Please give units on the x-axis in Fig. 2C?
5. Fig. 3E: Consider re-arranging. It is not immediately clear that all five bar charts belong to this panel.
6. There is a typo in Fig. S4A - mainteined
7. Methods, lines 408 - 410: Please state units of the parameters used to estimate promoter activity.

Referee Cross-Commenting

I agree with reviewer #1's assessment of significance and their reservation regarding the conclusion "ERK activity is required to maintain Oct4 expression in the naïve to formative pluripotency transition". The experiment that the reviewer suggests is reasonable and doable (see also my major point 4.). Even though reviewer #1 has not explicitly commented on the conclusions drawn from Fig. 2, I disagree with their assessment that these conclusions are convincing (see my major point 2.).

Significance

The control of pluripotency transitions by signaling mechanisms as well as transcription factor circuits have been mapped in quite some detail over the last decade. The main advance of this manuscript is that it looks at the interaction between these two levels and thereby provides some new and interesting links. These results will mainly be of interest to a large community of researchers working with pluripotent stem cells. To me, the most intriguing finding of the paper is the indeterminate cell state that the authors detect upon combined Nanog knockdown and MEK inhibition. To my knowledge, such a dead end of differentiation has not been reported before, at least not with pluripotent cells. This result could be a starting point for further investigation, and is of potential interest to a broader stem cell community.

Expertise: As a stem cell biologist I have the expertise to evaluate all parts of the paper.

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

Summary:

In this manuscript, the authors investigated the role of Erk signaling in the transition from naïve to formative pluripotency. They found that Erk activation eliminates Nanog to allow naïve state exit. However, when Nanog is knocked down in the absence of Erk activation, ESCs exit the naïve state, and enter an indetermined state, unable to proceed to the formative state. The authors further claimed that the failure to the formative state is due to lack of Oct4 expression. In conclusion, Erk signaling is required for the exit from the naïve state and the entry to the formative state.

Major comments:

• Are the key conclusions convincing? Most of the key conclusions are convincing, except for the conclusion "ERK activity is required to maintain Oct4 expression in the naïve to formative pluripotency transition". The authors showed that Oct4 expression is diminished under the MEK(i)+siNanog condition, while Oct4 is expressed in N2B27+siNeg (Figure 4C). With these experimental setting, the conclusion that ERK activity is required to maintain Oct4 expression in the naïve to formative pluripotency transition, cannot be reached, because two variations, MEK(i) and siNanog, rather than one variation MEK(i), are there. The experiment should be designed as adding MEK(i) into N2B27+siNeg at various time points, to test whether MEK(i) is able to down-regulate Oct4 expression in the naïve to formative pluripotency transition.
• 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.

The suggested experiment was described above. - 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.

It should not cost too much in terms of funding and time. - 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?

Statistical analysis is lacking for Figure 3E and Figure 4.

Minor comments:

• Specific experimental issues that are easily addressable.

No. - 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?

No.

Significance

This work characterized the role of ERK signaling in the transition between naïve and formative pluripotency. The function of ERK in ESC self-renewal and differentiation has been well recognized. Thus, this work provides new discoveries, but no conceptual advances. It should be of interest to a specialized audience in the pluripotency field, which is my expertise.

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

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Reply to the reviewers

Dear Dr. Sara Monaco,

Thank you very much for your kind e-mail dated 1-Feb-2024. Please find enclosed our revised version and our point-by-point reply to the comments from the reviewers. We have answered all major and minor points raised by the reviewers. Original Figures and Supplementary Figures were revised and renamed as follows.

Figure 1 -> Figure 1 and Revised Figure 2

Figure 2 -> Revised Figure 3 and Supplementary Figure 7

Figure 3 -> Revised Figure 4

Figure 4 -> Revised Figure 5 and 6

Figure 5 -> Revised Figure 7

Figure 6 -> Revised Figure 8

Supplementary Figure 1 -> Supplementary Figure 1

Supplementary Figure 2 -> Revised Supplementary Figure 3

Supplementary Figure 3 -> Revised Supplementary Figure 4

Supplementary Figure 4 -> Revised Figure 2

Supplementary Figure 5 -> Revised Supplementary Figure 6

Supplementary Figure 6 -> Revised Supplementary Figure 9

Supplementary Figure 7 -> Revised Supplementary Figure 10

Supplementary Figure 8 -> Revised Supplementary Figure 11

Supplementary Figure 9 -> Revised Supplementary Figure 12

We believe that our revised manuscript has been significantly improved thanks to your help. Thank you very much again for your help.

Yours sincerely,

Yosuke Mai and Ken Natsuga

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

SUMMARY In this study, the researchers investigate the spontaneous patterning of keratinocytes. As model they use HaCaT cells, an immortalized keratinocyte line. The cells exhibit a self-organized pattern of high and low cell density, which is disrupted by medium changes but reappear over time. The researchers find that serum starvation and high calcium concentration are crucial for the formation of these keratinocyte patterns. RNA sequencing analysis of regions of high vs low density indicates enrichment in gene ontology terms related to cell-cell adhesion, mainly adherens junctions (AJs), and keratinocyte differentiation. Experimental manipulations, such as inhibiting E-cadherin- or α-catenin-mediated adhesion, and disrupting myosin-II activity, all interfer with the formation of keratinocyte patterns, emphasizing the importance of AJs. Mathematical modeling suggests that cell-cell adhesion alone is sufficient for the emergence of density patterns. Keratinocyte patterns have spatial regulation of keratinocyte differentiation and proliferation. Differentiated cells are abundant in areas of high cell density, while proliferative cells are in areas of low cell density. The authors verify that YAP activity regulates pattern-dependent differentiation and proliferation. The role of serum starvation and cell-cell adhesion through AJs in the differentiation of keratinocytes are supported by epidermal stratification experiments in 3D culture, and ex vivo experiments on mouse skin suction blister wounds. In conclusion, the study provide insights into the spatial regulation of differentiation and proliferation in epidermal cells. MAJOR COMMENTS Although not novel, given that it has been already demonstrated with several other epithelial cell monolayers and in vivo in Drosophila, the conclusions that serum starvation facilitates epidermal stratification through cell-cell adhesion is convincing. It is unclear whether the cell patterning the authors are describing is a real patterning, defined in biology as any regularly repeated cell or structural arrangement or simply an inhomogeneous distribution of cell densities.*

We have addressed this issue by analyzing our images with the autocorrelation function (see Fig. 1g, 1h, and Supplementary Fig. 5) and confirmed that the distribution of high/low cell density is patterned with the average nearest neighbor distance between areas of high cell density being approximately 300 µm. We have incorporated these new data into the revised manuscript.

The conclusion that the cell-cell adhesion signaling pathway identified in the paper "might promote wound healing in clinical settings" (last sentence of the abstract) is not substantiated by the results.

We agree with the reviewer's point and have deleted the sentence in the abstract, accordingly.

It would be opportune to better describe the type of "cell patterning" that the authors are seeing in their experiments. In my opinion the effect seen in the described experiment is not a "patterning" but a difference in cell density which can be less or more homogeneous in an HaCat monolayer.

Please see the answer above on our analysis using the autocorrelation function.

Importantly, it is unclear whether the "cell patterning" is a subsequent consequence or proceed stratification.

As the mathematical modeling indicated patterning without the need for stratification steps, we believe that cell patterning is not a direct consequence of stratification. However, it is technically difficult to differentiate whether patterning developed prior to stratification in our experimental settings. We have added this limitation to the Discussion of the revised manuscript.

It is unclear how starvation relates to the increased adhesions and YAP signaling.

As the reviewer pointed out, we could not address what molecules in the serum are responsible because the serum is a complex mixture of biomolecules that includes hormones, growth factors, vitamins, and other nutrients. We have added this limitation of our study to the revised manuscript.

The authors conclude the discussion section proposing "that molecules involved in cell-cell adhesion-induced patterning are suitable target candidates to facilitate wound healing". None the experiments done in the wound healing setting are addressing the role of any molecules described in the paper. I would suggest the authors to remove this last claim from the manuscript. Alternatively, the authors should provide evidence that targeting some of the molecules described in the manuscript are accelerating wound healing in a clinically relevant model of wound healing.

We agree with the reviewer's point and have deleted the passage in the revised manuscript, accordingly.

I would request the authors to provide the following essential data to substantiate their experiments: - Provide a full gene list related to Figure 2a.

We have provided the gene list (Supplementary Table 1), accordingly.

- In relation to Figure 2c, stain for a-catenin and quantify the intensity ration of a-catenin vs a-18-catenin as proper readout of adhesion strength (see Yonemura et al., Nat Cell Biol 2010).

As the reviewer pointed out, the intensity ratio of α-catenin vs. α18 is a general readout of cell adhesion strength. However, this ratio should be based on similar intensity of alpha catenin between two groups for comparison. In contrast, the intensity of α-catenin itself was weaker in the area with low cell density compared with in that with high cell density in our experimental setting (Supplementary Fig. 8d, e, g), which could greatly affect the ratio. To overcome this problem, we have reanalyzed line plots of α-catenin immunofluorescence, picked up the α18 intensity at the peaks (corresponding to cell-cell adhesion) of α-catenin, and compared that of high and low cell density area. As expected, α18 was more pronounced in the area with high cell density. We have added the data to Supplementary Fig. 8d-h in the revised manuscript.

- Properly quantify nuclear vs cytoplasmic localization of YAP in low vs high density areas in Figure 4f.

According to the reviewer's suggestion, we have quantified nuclear/cytoplasmic YAP and added the data (Revised Fig. 6b (original Fig. 4)) to the revised manuscript.

• The nuclear localization of YAP is not sufficient to demonstrate activation of the YAP signaling. The authors should provide evidence of YAP activity in low vs high density areas looking for example at known downstream target genes in epithelial cells (see Zhao et al., Genes Dev 2007; Yu et al., Cell 2012; Aragona et al., Cell 2013).

We have analyzed ANKRD1 (Yu et al., Cell 2012) as a YAP readout molecule and confirmed that, in line with YAP dynamics, ANKRD1 was localized in the nucleus of high cell density area. We have provided the data (Revised Fig. 6c, d (original Fig. 4)) for the revised manuscript.

• The activity of PY-60 in Figure 4g and XAV939 in Figure 4i as YAP activator and repressor respectively, should be controlled against YAP localization and activity.

We have quantitatively analyzed YAP and ANKRD1 localization upon chemical treatment and added the data (Supplementary Fig. 1a-d, g-j (original Supplementary Fig. 8)) to the revised manuscript.

• In Figure 5a a quantification of the numbers of cell layers should be used instead of the thickness and a staining and quantification of K14 and K10 should be added to formally address stratification.

As expected, the number of K10-positive cell layers was larger in serum-starved conditions than in serum-rich conditions, while the number of K14-positive cell layer was comparable between the two groups. We have provided the quantification data (Supplementary Fig. 12 c-e (original Supplementary Fig. 9)) to the revised manuscript accordingly.

*Most of the proposed experiments are simply additional quantifications of images or adjustments of data that are already available to the authors. I estimate that the remaining experiments can be done in less than a month and will not require additional expertise.

The methods, figures presentation and legends, and the statistical analysis are adequate, clear and accurate.

MINOR COMMENTS There are three fundamental studies that the authors should discuss: - Saw, Doostmohammadi et al., Nature 2017. Topological defects in epithelia govern cell death and extrusion. Here, the role of topological defects (see also Bonn et al., Phys Res E 2022) and a-catenin-dependent cell-cell interactions are connected to cell extrusion and Yap activity in epithelial monolayers including HaCat cells. - Miroshnikova et al., Nat Cell Biol 2018. Adhesion forces and cortical tension couple cell proliferation and differentiation to direct epidermal stratification. Here, the authors demonstrated that the increase of cell-cell adhesion couples with a decrease of cortical tension triggers stratification in the skin epidermis. - Boocock et al., Nature Physics 2021. Theory of mechanochemical patterning and optimal migration in cell monolayers. Here, cell density and ERK activity are formalized to be key players in patterning formation in a cell monolayer. In addition, several components of the Hippo-YAP pathway are known regulators of cell-cell adhesion (e.g. AMOT and NF2) and should be discussed (for reference see reviews on the topic Zheng & Pan, Dev Cell 2019; Karaman & Halder Cold Spring Harb Perspect Biol 2018; Gumbiner & Kim, J Cell Sci 2014) as important molecules implicated in the biological phenomena described in the manuscript.0*

We appreciate the reviewer's suggestion and have cited and discussed these seminal papers in the revised manuscript.

Reviewer #1 (Significance (Required)):

The study aims at understanding spontaneous patterning of keratinocytes. The authors nicely employ various experimental approaches, including cell imaging, RNA sequencing, cell manipulation by genetic engineering and pharmacological treatments, and mathematical modeling, to elucidate the underlying cellular and molecular mechanisms regulating this proces. However, several of the conclusions presented in the manuscript do not present any conceptual advance to the field of self-organization of cell density patterns or epithelial biology.

The role of starvation in effecting epithelial growth is very well known. The role of AJ in pattern formation has been described previously in epithelial monolayers (Saw, Doostmohammadi et al., Nature 2017) and in vivo in Drosophila (Mao et al., Genes Dev 2011; Mao et al., EMBO J 2013). The effect of cell density on YAP signaling is known (Zhao et al., Genes Dev 2007; Aragona et al., Cell 2013). The importance of AJ for keratinocytes differentiation and stratification has been demonstrated in vitro and in vivo (Miroshnikova et al., Nat Cell Biol 2018). The role of a-catenin upstream of YAP activity in regulating interfollicular epidermis stem cells self-renewal and wound healing has been demonstrated in vitro and in vivo by the group of Fernando Camargo in Cell 2011.

The manuscript could be of interest for researchers interested in basic cell biology and a specialised audience in cell self-organisation.

My field of expertise: epithelial biology, stem cell biology, skin homeostasis and wound healing, mechanobiology, YAP signaling. I do not have sufficient expertise to evaluate the mathematical modelling.

We appreciate the reviewer's constructive comments.

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

Summary:

Mai et al. reported an interesting observation that serum starvation induced the keratinocytes, a type of epithelial cells, to form a pattern characterized by regions with high and low densities. They showed that this patterning processing depends on cell-cell adhesion using a series of pharmacological treatment and a CRISPR knockout of alpha-catenin. They used mathematical modeling to demonstrate that cell-density dependent stress can sufficiently generate patterns of high and low cell densities, but the interpretation of the modeling is questionable (see below). They showed correlation of a differentiated keratinocyte marker, keratin 10, with the high-density region, but over claimed this result as patterning modulates differentiation. They also showed correlation of YAP activity (cytoplasmic to nuclear ratio) to the high vs. low-density regions. Interestingly, treatment with a YAP activator PY-60 disrupted pattern formation, while the YAP inhibitor XAV939 barely affected pattern formation. Finally, the authors demonstrated that serum starvation increased the thickness of keratinocytes cultured in a trans-well system (which they called 3D culture), and a mouse back skin explant compared to serum-rich culture conditions. In the former system, they showed dependence on alpha-catenin using the CRISPR knockout.

Major comments:

The conclusion that "mathematical modeling indicates that cell-cell adhesion alone is sufficient to form regions with high/low cell density" is misleading. The key assumption of the modeling is that the time derivative of stress (d_sigma/dt) is proportional to the cell density (rho), where the proportion parameter (beta) was interpreted as cell adhesion strength. However, beta could be interpreted as any general attractor proportional to the cell density, such as a chemoattractant.*

Our purpose here is to demonstrate that the model based on the assumption of cell-cell adhesion as a mere source of attractive forces can reproduce the experimentally observed spatial patterning. As the referee rightly points out, the term beta*rho in the second equation allows different interpretations such as the effect of attractant proportional to cell density. Therefore, our mathematical model cannot be used as a proof of the existence of cell-cell adhesion. We have reduced the tone in the revised manuscript.

In addition, it is unclear why the time derivative of stress (d_sigma/dt) instead of stress itself (sigma) proportional to the cell density. The authors should further clarify the meanings of modeling parameters and be more careful with their conclusions.

If the system is in the steady state (d_sigma/dt = 0) with no spatial variations (nabla^2 \sigma = 0), then the second equation reduces to sigma = (beta/alpha) rho, namely that the cell density is proportional to stress, as pointed out by the referee.

Our model, which describes temporal and spatial variations, generalizes this situation. The spatial dependence represented by nabla^2 sigma was introduced according to the Reference 72 (original Reference 51). Furthermore, we introduced the time derivative d_sigma/dt to account for the fact that the system should relax into the steady state described above. We have included these into the revised manuscript.

Related to above, the authors should revise the title to reflect that the patterning depends on cell-cell adhesion instead of claiming that cell-cell adhesion drives patterning. This would require experimentally demonstrating sufficiency, for example, showing that increasing adhesion in a cell line with low adhesion that does not show patterning can sufficiently induce patterning.

We agreed with the reviewer and have revised the title into "Patterning in stratified epithelia depends on cell-cell adhesion" and reduce the tone of the final sentence of the Discussion section accordingly.

The conclusion that "patterning modulates differentiation" is not supported by evidence. Differentiation as evidenced by the presence of keratin 10 occurred as early as day 2 before any signs of patterning (Fig. 4A). When patterning was completely disrupted by alpha-catenin KO, there are still many keratin 10 positive cells. The apparent higher proportion of keratin 10+ cells in the wild type seems to be merely reflecting the higher cell density - if the quantification were normalized by the cell number, they are probably comparable. Overall, the presented data only supports a correlation of the differentiation marker keratin 10 with high-density regions.

According to the reviewer's suggestion, we have reduced the tone of the title of Revised Fig. 4 (original Fig. 3) and changed it into "Patterning correlates with differentiation and proliferation markers in keratinocytes".

The choice of RNA-seq comparison groups (high-density vs. low-density culture) is puzzling, since the effects caused by culture density changes may not be related to the high vs. low-density regions in the patterned cultures. There are so many changes there and the rationale of following up on cell adhesion was unclear. In fact, it seems that the RNA-seq data didn't help the logic flow of the paper at all.

Although we believe that comparison between high-density and low-density culture partly recapitulates high/low cell density regions in our study, the comparison is not identical to patterned cultures as the reviewer pointed out. We have moved RNA-seq data to the Supplementary Information (Supplementary Fig. 7) and added more analysis to address that cell adhesion and differentiation are major differences between high-density and low-density culture, supporting further analysis on this matter in our study.

The claim of 3D culture of keratinocytes is confusing. The culture in the trans-well insert is still on the flat 2D surface, why should it be called 3D culture? If the point is to culture at air/liquid interface, that should instead be emphasized instead of calling it 3D.

We have changed "3D culture" into air-liquid interface culture, accordingly.

Reviewer #2 (Significance (Required)):

The observation that serum starvation and replenishment induced reversible patterning of the keratinocytes is quite interesting. However, the biological relevance is unclear - isn't all skin stratified? The evidence supporting the dependence of this patterning on adherens junction by disrupting E-cadherin, myosin, or alpha-catenin is convincing, although not surprising. The involvement of YAP in differentiation vs. proliferation is interesting, but it's in line with the known functions of YAP. The modeling part, with some clarification, can be quite insightful. Overall, this research could be interesting to those working in epithelial morphogenesis, if further developed.

My expertise is in epithelial tissue morphogenesis, mechanobiology, and extracellular matrix biology.

We appreciate the reviewer's constructive and thoughtful comments.

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

In this manuscript the authors aim to understand the signals that coordinate spatial patterns of keratinocyte proliferation and differentiation. To address this question the authors use the HaCaT keratinocyte cell line that upon serum starvation forms spatially separated domains of proliferation and differentiation. The data presented in this manuscript potentially suggest that serum starvation works through adherens junctions to create differentially dense fields within the cultures which determines whether cells proliferate or differentiate. The authors then perform experiments to show that junction formation with starvation drive keratinocyte differentiation potentially through YAP signaling. However, these experiments are rather loosely connected and their results often do not support the conclusions drawn by the authors. However, the not well supported conclusion the form the basis for a fact statement, but their data really did not show that. For example, the authors state: "By contrast, YAP inhibition by a tankyrase inhibitor, XAV939, suppressed pattern-dependent proliferation (Fig. 4i, j)," . However, their data do not show that proliferation is pattern-dependent but is nevertheless used to connect to and draw a conclusion about YAP signaling. The data itself appear to be of high quality, figures are well organized and statistics of quantification seem appropriate, but it somewhat problematic that throughout the manuscript it remains unclear if certain statements are hypotheses or conclusions on real data. Pattern formation as a requirement for differentiation is an interesting concept. However, the presented study lacks proper conclusive data how these patterns may contribute to proliferation and differentiation and remains rather short on what exactly is the instructive nature of these patterns, as they only use high density and are not generating own patterns with defined cues that explore what cues contribute. Major points: The statement "According to the RNA-seq data, AJ molecules, such as E-cadherin and actin, were localized at intercellular junctions in areas of high cell density" is not correct. RNA-seq does not allow conclusions about protein localization. Instead, the GO-Term analysis shown in Figure 2b shows downregulation of "cell-adhesion" in dense areas. *

According to the reviewer's suggestion, we have corrected the sentence. We have reanalyzed our RNA-seq data and confirmed that GO-term "cell-adhesion" was in the top list of both high and low cell density regions. We have provided more data to the revised manuscript (Supplementary Fig. 7 and Supplementary Table 1).

*Consistently the E-cadherin staining presented in Figure2c suggest lower intercellular E-cadherin levels in the most dense areas. However, any statement about junctional localization of adhesion components requires e.g. intensity quantification at junctions vs. cytoplasm or else to discriminate from intense overall staining due to high cell density and thus high overall junction numbers. *

Actually, junctional E-cadherin was more pronounced in the high cell density area. We have provided line plot data to confirm this and also added a quantification data (Supplementary Fig. 8).

Hence, even though potentially true, the statement: "These data suggest that cells in regions of high cell density form AJs in response to intercellular forces" is not fully supported by the data shown so far.

Please see the answer to the comments of Reviewer 1 on the quantification of α18. We believe that, as α18 intensity is more pronounced in the cell-cell junction of high cell density area compared with low cell density regions, our claim is experimentally supported.

The authors suggest a pattern of high and low density that is formed over time. However, at the same time high density areas show formation of a second layer. Hence, "denser" areas as observed by phase contrast images or DAPI positive nuclei may either represent dense or stratified cells. What is missing is an analysis of cell density before cells started to stratify making sure only cells in the basal layer are analyzed. Otherwise, density and stratification which are perhaps interdependent in this system cannot be discriminated.

As the reviewer pointed out, the patterning was analyzed at the level of basal layer. In addition to Figure 1c, we have provided another plane cut immunofluorescence data (Supplementary Fig. 2) to the revised manuscript to address this issue.

*The mathematical model does not include stratification and it is thus not clear to what extend it may explain the observed patterns. *

It is true that the model does not account for stratification. It focuses solely on the patterning of cell density in the basal layer. We have incorporated this notion into the revised manuscript as a limitation of this study.

*Moreover, the model appears to assume variables that have not been determined or cited. This reviewer is not an expert in modeling and thus cannot fully judge the math behind the model. However, the model appears to be biased if it assumes, as mentioned, that cell-adhesion increases with density. *

The first equation, describing the time evolution of rho (the cell density), incorporates diffusion, collective cell movement due to stress from adjacent cells, and random fluctuations. Each of these terms comes from a general consideration of density dynamics. The second equation, describing stress balance, is a generalization of Reference 72 (originally Reference 51). The crucial assumption here is that the cell-cell adhesion increases with density, which corresponds to the experimental findings (Revised Fig. 3a, b, Supplementary Figure 8a-h).

What we have demonstrated here is that we only need cell-cell adhesion as a source of attractive interactions for cells to form the density patterning as observed in the experiment. Since it is not self-evident whether the assumption of the density-dependent adhesion entail the emergence of density patterns, we do not believe that our model is begging the question or biased.

*If low adhesion forces do not produce patterns, what is the counterforce in the model? Are cells allowed to change size to enable low density areas or do cells lose contact with neighbors despite high adhesion strength? *

Our model does not have a variable corresponding to cell-shape change, which is considered only implicitly: Cells in the low density region (small rho) are regarded as flattened, whereas those in the high density region (large rho) as compressed (though not stratified) (Fig 1c).

The behavior of the model is controlled by the parameter beta: a smaller beta means that density variations have little effect on stress, whereas a larger beta leads to significant stress changes with density variation. Since stress increases as beta*rho (in the second equation), stress in the low density region remains low even when the parameter beta is large.

Overall, it appears that the model is set up such, that it tends to reproduce what was observed in experiment. This conclusion, however, may result of an incomplete understanding of the model parameters.

The model setup, the assumption on the relationship between density and cell-cell adhesion in particular, does not inherently dictate the emergence of high/low density patterns: It might be the case that cell density is uniformly distributed everywhere with uniformly strong adhesion among cells. What our computer simulations have shown, however, is that the model exhibits spatially heterogeneous density patterns for sufficiently high beta values. The emergence of such spatial patterns is not a predefined aspect of the mathematical model itself.

In the revised manuscript, the non-triviality of the spatial patterning has been made clear in the Results, and more explanations on the mathematical model to address the above points have been added to the Methods section.

If dense areas do actually represent stratified areas it may not be surprising that the GO analysis indicates an increase in differentiation. A requirement for AJ or intercellular junctions in general is less surprising as stratification requires cell-cell adhesion. The observation that AJ are essential for intercellular junction formation in keratinocytes or in other epithelial cells is not new (e.g. Michels et al. JID 2009).

We agree with the reviewer in the point that the role of AJ is not new. We have incorporated the notion into the Discussion of the revised manuscript and cited the paper the reviewer indicated.

The part of the paper addressing the role of YAP suffers from a number of potentially mislead assumptions/conclusions based on a previous experiment which then did not properly supported that conclusion (see also overall comments). For example, the statement "YAP inhibition by a tankyrase inhibitor, XAV939, suppressed pattern-dependent proliferation" contains interdependencies that have not been show [sic]. XAV939 may just inhibit proliferation which is not necessarily pattern dependent. Too much speculation confuses data and hypotheses.

We agree with the reviewer to point out that pattern-dependency was not supported by our results. We have reduced the tones and corrected these terms in the revised manuscript.

The 3D HaCaT cultures are performed on transwell filters with medium supply above and below cells, with the assumption that organizing patterns are also formed under these conditions. However, this has not been shown by the authors. Their suggestion that serum starvation may increases thickness of cultures through alterations in the organization of [sic]

We showed the patterning in air-liquid interface culture in the Supplementary Data (Supplementary Fig. 12a, b, original Supplementary Fig. 9a, b), which presents starvation-induced pattering even in such condition.

Reviewer #3 (Significance (Required)):

The mechanisms that drive self-organization of epithelial cells to spatially separate domains of proliferation and differentiation is in principle a very interesting topic of high interest to the cell and mechanobiology community, [sic]

We appreciate the reviewer's constructive and thoughtful comments.

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

Learn more at Review Commons

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Referee #3

Evidence, reproducibility and clarity

In this manuscript the authors aim to understand the signals that coordinate spatial patterns of keratinocyte proliferation and differentiation. To address this question the authors use the HaCaT keratinocyte cell line that upon serum starvation forms spatially separated domains of proliferation and differentiation. The data presented in this manuscript potentially suggest that serum starvation works through adherens junctions to create differentially dense fields within the cultures which determines whether cells proliferate or differentiate. The authors then perform experiments to show that junction formation with starvation drive keratinocyte differentiation potentially through YAP signaling. However, these experiments are rather loosely connected and their results often do not support the conclusions drawn by the authors. However, the not well supported conclusion the form the basis for a fact statement, but their data really did not show that. For example, the authors state: "By contrast, YAP inhibition by a tankyrase inhibitor, XAV939, suppressed pattern-dependent proliferation (Fig. 4i, j)," . However, their data do not show that proliferation is pattern-dependent but is nevertheless used to connect to and draw a conclusion about YAP signaling. The data itself appear to be of high quality, figures are well organized and statistics of quantification seem appropriate, but it somewhat problematic that throughout the manuscript it remains unclear if certain statements are hypotheses or conclusions on real data. Pattern formation as a requirement for differentiation is an interesting concept. However, the presented study lacks proper conclusive data how these patterns may contribute to proliferation and differentiation and remains rather short on what exactly is the instructive nature of these patterns, as they only use high density and are not generating own patterns with defined cues that explore what cues contribute.

Major points:

The statement "According to the RNA-seq data, AJ molecules, such as E-cadherin and actin, were localized at intercellular junctions in areas of high cell density" is not correct. RNA-seq does not allow conclusions about protein localization. Instead, the GO-Term analysis shown in Figure 2b shows downregulation of "cell-adhesion" in dense areas. Consistently the E-cadherin staining presented in Figure2c suggest lower intercellular E-cadherin levels in the most dense areas. However, any statement about junctional localization of adhesion components requires e.g. intensity quantification at junctions vs. cytoplasm or else to discriminate from intense overall staining due to high cell density and thus high overall junction numbers. Hence, even though potentially true, the statement: "These data suggest that cells in regions of high cell density form AJs in response to intercellular forces" is not fully supported by the data shown so far. The authors suggest a pattern of high and low density that is formed over time. However, at the same time high density areas show formation of a second layer. Hence, "denser" areas as observed by phase contrast images or DAPI positive nuclei may either represent dense or stratified cells. What is missing is an analysis of cell density before cells started to stratify making sure only cells in the basal layer are analyzed. Otherwise, density and stratification which are perhaps interdependent in this system cannot be discriminated. The mathematical model does not include stratification and it is thus not clear to what extend it may explain the observed patterns. Moreover, the model appears to assume variables that have not been determined or cited. This reviewer is not an expert in modeling and thus cannot fully judge the math behind the model. However, the model appears to be biased if it assumes, as mentioned, that cell-adhesion increases with density. If low adhesion forces do not produce patterns, what is the counterforce in the model? Are cells allowed to change size to enable low density areas or do cells lose contact with neighbors despite high adhesion strength? Overall, it appears that the model is set up such, that it tends to reproduce what was observed in experiment. This conclusion, however, may result of an incomplete understanding of the model parameters. If dense areas do actually represent stratified areas it may not be surprising that the GO analysis indicates an increase in differentiation. A requirement for AJ or intercellular junctions in general is less surprising as stratification requires cell-cell adhesion. The observation that AJ are essential for intercellular junction formation in keratinocytes or in other epithelial cells is not new (e.g. Michels et al. JID 2009).

The part of the paper addressing the role of YAP suffers from a number of potentially mislead assumptions/conclusions based on a previous experiment which then did not properly supported that conclusion (see also overall comments). For example, the statement "YAP inhibition by a tankyrase inhibitor, XAV939, suppressed pattern-dependent proliferation" contains interdependencies that have not been show. XAV939 may just inhibit proliferation which is not necessarily pattern dependent. Too much speculation confuses data and hypotheses.

The 3D HaCaT cultures are performed on transwell filters with medium supply above and below cells, with the assumption that organizing patterns are also formed under these conditions. However, this has not been shown by the authors. Their suggestion that serum starvation may increases thickness of cultures through alterations in the organization of

Significance

The mechanisms that drive self-organization of epithelial cells to spatially separate domains of proliferation and differentiation is in principle a very interesting topic of high interest to the cell and mechanobiology community,

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:

Mai et al. reported an interesting observation that serum starvation induced the keratinocytes, a type of epithelial cells, to form a pattern characterized by regions with high and low densities. They showed that this patterning processing depends on cell-cell adhesion using a series of pharmacological treatment and a CRISPR knockout of alpha-catenin. They used mathematical modeling to demonstrate that cell-density dependent stress can sufficiently generate patterns of high and low cell densities, but the interpretation of the modeling is questionable (see below). They showed correlation of a differentiated keratinocyte marker, keratin 10, with the high-density region, but over claimed this result as patterning modulates differentiation. They also showed correlation of YAP activity (cytoplasmic to nuclear ratio) to the high vs. low-density regions. Interestingly, treatment with a YAP activator PY-60 disrupted pattern formation, while the YAP inhibitor XAV939 barely affected pattern formation. Finally, the authors demonstrated that serum starvation increased the thickness of keratinocytes cultured in a trans-well system (which they called 3D culture), and a mouse back skin explant compared to serum-rich culture conditions. In the former system, they showed dependence on alpha-catenin using the CRISPR knockout.

Major comments:

The conclusion that "mathematical modeling indicates that cell-cell adhesion alone is sufficient to form regions with high/low cell density" is misleading. The key assumption of the modeling is that the time derivative of stress (d_sigma/dt) is proportional to the cell density (rho), where the proportion parameter (beta) was interpreted as cell adhesion strength. However, beta could be interpreted as any general attractor proportional to the cell density, such as a chemoattractant. In addition, it is unclear why the time derivative of stress (d_sigma/dt) instead of stress itself (sigma) proportional to the cell density. The authors should further clarify the meanings of modeling parameters and be more careful with their conclusions.

Related to above, the authors should revise the title to reflect that the patterning depends on cell-cell adhesion instead of claiming that cell-cell adhesion drives patterning. This would require experimentally demonstrating sufficiency, for example, showing that increasing adhesion in a cell line with low adhesion that does not show patterning can sufficiently induce patterning.

The conclusion that "patterning modulates differentiation" is not supported by evidence. Differentiation as evidenced by the presence of keratin 10 occurred as early as day 2 before any signs of patterning (Fig. 4A). When patterning was completely disrupted by alpha-catenin KO, there are still many keratin 10 positive cells. The apparent higher proportion of keratin 10+ cells in the wild type seems to be merely reflecting the higher cell density - if the quantification were normalized by the cell number, they are probably comparable. Overall, the presented data only supports a correlation of the differentiation marker keratin 10 with high-density regions.

The choice of RNA-seq comparison groups (high-density vs. low-density culture) is puzzling, since the effects caused by culture density changes may not be related to the high vs. low-density regions in the patterned cultures. There are so many changes there and the rationale of following up on cell adhesion was unclear. In fact, it seems that the RNA-seq data didn't help the logic flow of the paper at all.

The claim of 3D culture of keratinocytes is confusing. The culture in the trans-well insert is still on the flat 2D surface, why should it be called 3D culture? If the point is to culture at air/liquid interface, that should instead be emphasized instead of calling it 3D.

Significance

The observation that serum starvation and replenishment induced reversible patterning of the keratinocytes is quite interesting. However, the biological relevance is unclear - isn't all skin stratified? The evidence supporting the dependence of this patterning on adherens junction by disrupting E-cadherin, myosin, or alpha-catenin is convincing, although not surprising. The involvement of YAP in differentiation vs. proliferation is interesting, but it's in line with the known functions of YAP. The modeling part, with some clarification, can be quite insightful. Overall, this research could be interesting to those working in epithelial morphogenesis, if further developed.

My expertise is in epithelial tissue morphogenesis, mechanobiology, and extracellular matrix biology.

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Referee #1

Evidence, reproducibility and clarity

Summary

In this study, the researchers investigate the spontaneous patterning of keratinocytes. As model they use HaCaT cells, an immortalized keratinocyte line. The cells exhibit a self-organized pattern of high and low cell density, which is disrupted by medium changes but reappear over time. The researchers find that serum starvation and high calcium concentration are crucial for the formation of these keratinocyte patterns. RNA sequencing analysis of regions of high vs low density indicates enrichment in gene ontology terms related to cell-cell adhesion, mainly adherens junctions (AJs), and keratinocyte differentiation. Experimental manipulations, such as inhibiting E-cadherin- or α-catenin-mediated adhesion, and disrupting myosin-II activity, all interfer with the formation of keratinocyte patterns, emphasizing the importance of AJs. Mathematical modeling suggests that cell-cell adhesion alone is sufficient for the emergence of density patterns. Keratinocyte patterns have spatial regulation of keratinocyte differentiation and proliferation. Differentiated cells are abundant in areas of high cell density, while proliferative cells are in areas of low cell density. The authors verify that YAP activity regulates pattern-dependent differentiation and proliferation. The role of serum starvation and cell-cell adhesion through AJs in the differentiation of keratinocytes are supported by epidermal stratification experiments in 3D culture, and ex vivo experiments on mouse skin suction blister wounds.

In conclusion, the study provide insights into the spatial regulation of differentiation and proliferation in epidermal cells.

Major comments

Although not novel, given that it has been already demonstrated with several other epithelial cell monolayers and in vivo in Drosophila, the conclusions that serum starvation facilitates epidermal stratification through cell-cell adhesion is convincing. It is unclear whether the cell patterning the authors are describing is a real patterning, defined in biology as any regularly repeated cell or structural arrangement or simply an inhomogeneous distribution of cell densities. The conclusion that the cell-cell adhesion signaling pathway identified in the paper "might promote wound healing in clinical settings" (last sentence of the abstract) is not substantiated by the results.

It would be opportune to better describe the type of "cell patterning" that the authors are seeing in their experiments. In my opinion the effect seen in the described experiment is not a "patterning" but a difference in cell density which can be less or more homogeneous in an HaCat monolayer.

Importantly, it is unclear whether the "cell patterning" is a subsequent consequence or proceed stratification. It is unclear how starvation relates to the increased adhesions and YAP signaling. The authors conclude the discussion section proposing "that molecules involved in cell-cell adhesion-induced patterning are suitable target candidates to facilitate wound healing". None the experiments done in the wound healing setting are addressing the role of any molecules described in the paper. I would suggest the authors to remove this last claim from the manuscript. Alternatively, the authors should provide evidence that targeting some of the molecules described in the manuscript are accelerating wound healing in a clinically relevant model of wound healing.

I would request the authors to provide the following essential data to substantiate their experiments:

• Provide a full gene list related to Figure 2a.
• In relation to Figure 2c, stain for a-catenin and quantify the intensity ration of a-catenin vs a-18-catenin as proper readout of adhesion strength (see Yonemura et al., Nat Cell Biol 2010).
• Properly quantify nuclear vs cytoplasmic localization of YAP in low vs high density areas in Figure 4f.
• The nuclear localization of YAP is not sufficient to demonstrate activation of the YAP signaling. The authors should provide evidence of YAP activity in low vs high density areas looking for example at known downstream target genes in epithelial cells (see Zhao et al., Genes Dev 2007; Yu et al., Cell 2012; Aragona et al., Cell 2013).
• The activity of PY-60 in Figure 4g and XAV939 in Figure 4i as YAP activator and repressor respectively, should be controlled against YAP localization and activity.
• In Figure 5a a quantification of the numbers of cell layers should be used instead of the thickness and a staining and quantification of K14 and K10 should be added to formally address stratification.

Most of the proposed experiments are simply additional quantifications of images or adjustments of data that are already available to the authors. I estimate that the remaining experiments can be done in less than a month and will not require additional expertise.

The methods, figures presentation and legends, and the statistical analysis are adequate, clear and accurate.

Minor comments

There are three fundamental studies that the authors should discuss:

• Saw, Doostmohammadi et al., Nature 2017. Topological defects in epithelia govern cell death and extrusion. Here, the role of topological defects (see also Bonn et al., Phys Res E 2022) and a-catenin-dependent cell-cell interactions are connected to cell extrusion and Yap activity in epithelial monolayers including HaCat cells.
• Miroshnikova et al., Nat Cell Biol 2018. Adhesion forces and cortical tension couple cell proliferation and differentiation to direct epidermal stratification. Here, the authors demonstrated that the increase of cell-cell adhesion couples with a decrease of cortical tension triggers stratification in the skin epidermis.
• Boocock et al., Nature Physics 2021. Theory of mechanochemical patterning and optimal migration in cell monolayers. Here, cell density and ERK activity are formalized to be key players in patterning formation in a cell monolayer.

In addition, several components of the Hippo-YAP pathway are known regulators of cell-cell adhesion (e.g. AMOT and NF2) and should be discussed (for reference see reviews on the topic Zheng & Pan, Dev Cell 2019; Karaman & Halder Cold Spring Harb Perspect Biol 2018; Gumbiner & Kim, J Cell Sci 2014) as important molecules implicated in the biological phenomena described in the manuscript.

Significance

The study aims at understanding spontaneous patterning of keratinocytes. The authors nicely employ various experimental approaches, including cell imaging, RNA sequencing, cell manipulation by genetic engineering and pharmacological treatments, and mathematical modeling, to elucidate the underlying cellular and molecular mechanisms regulating this proces. However, several of the conclusions presented in the manuscript do not present any conceptual advance to the field of self-organization of cell density patterns or epithelial biology.

The role of starvation in effecting epithelial growth is very well known. The role of AJ in pattern formation has been described previously in epithelial monolayers (Saw, Doostmohammadi et al., Nature 2017) and in vivo in Drosophila (Mao et al., Genes Dev 2011; Mao et al., EMBO J 2013). The effect of cell density on YAP signaling is known (Zhao et al., Genes Dev 2007; Aragona et al., Cell 2013). The importance of AJ for keratinocytes differentiation and stratification has been demonstrated in vitro and in vivo (Miroshnikova et al., Nat Cell Biol 2018). The role of a-catenin upstream of YAP activity in regulating interfollicular epidermis stem cells self-renewal and wound healing has been demonstrated in vitro and in vivo by the group of Fernando Camargo in Cell 2011.

The manuscript could be of interest for researchers interested in basic cell biology and a specialised audience in cell self-organisation.

My field of expertise: epithelial biology, stem cell biology, skin homeostasis and wound healing, mechanobiology, YAP signaling. I do not have sufficient expertise to evaluate the mathematical modelling.

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Reply to the reviewers

We thank all reviewers for their thorough assessment and constructive comments. We are glad that the reviewers appreciate that our findings are of interest to the nuclear transport field and that our extension of the use of the RITE methodology can be a valuable tool for the further characterization of NPCs that differ in composition and potentially function. In response to the reviewers’ comments, we have revised the text to incorporate their suggestions and improve overall readability and clarity. Furthermore, we propose to perform a set of additional experiments to address the reviewers’ most important critiques. Below we list our response with the reviewer comments reprinted in dark grey and our response in blue for easier orientation. We have added numbering of the comments for easier orientation.

Many of the comments made by the reviewers have already been implemented, additional points will be addressed in a revised version of the manuscript as detailed below.

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

The authors extended the existing recombination-induced tag exchange (RITE) technology to show that they can image a subset of NPCs, improving signal-to-noise ratios for live cell imaging in yeast, and to track the stability or dynamics of specific nuclear pore proteins across multiple cell divisions. Further, the authors use this technology to show that the nuclear basket proteins Mlp1, Mlp2 and Pml39 are stably associated with "old NPCs" through multiple cell cycles. The authors show that the presence of Mlp1 in these "old NPCs" correlates with exclusion of Mlp1-positive NPCs from the nucleolar territory. A surprising result is that basket-less NPCs can be excluded from the non-nucleolar region, an observation that correlates with the presence of Nup2 on the NPC regardless of maturation state of the NPC. In support of the proposal that retention of NPCs via Mlp1 and Nup2 in non-nucleolar regions, simulation data is presented to suggest that basket-less NPCs diffuse faster in the plane of the nuclear envelope.

However, there are some points that do need addressing:

Major Points 1. Taking into account that the Nup2 result in Figure 4B forms the basis for one half of the proposed model in Figure 6 regarding the exclusion of NPCs from the nucleolar region of the NE, there is a relatively small amount of data in support of this finding and this proposed model. For example, the only data for Nup2 in the manuscript is a column chart in Figure 4B with no supporting fluorescence microscopy examples for any Nup2 deletion. Further, the Nup60 deletion mutant will have zero basket-containing NPCs, whereas the Nup2 deletion will be a mixture of basket-containing and basket-less NPCs. The only support for the localization of basket-containing NPCs in the Nup2 deletion mutant is through a reference "Since Mlp1-positive NPCs remain excluded from the nucleolar territory in nup2Δ cells (Galy et al., 2004), the homogenous distribution observed in this mutant must be caused predominantly by the redistribution of Mlp-negative NPCs into the nucleolar territory."

We have already added fluorescent images of the nup2d strain to figure 4A in the preliminary revision.

In addition, we will repeat the experiment from Galy et al. 2004 to test whether Mlp-positive NPCs are excluded from nucleoli in our hands as well.

Furthermore, we propose to carry out more experiments to pinpoint which domains of Nup2 contribute to nucleolar exclusion, which will provide more insight into the mechanism behind this effect. We propose to do this by analyzing NPC localization in mutants expressing truncations of Nup2 with deletions for individual domains as their only copy of Nup2. Regardless of whether we find a single domain of Nup2 responsible of a combinatorial action, this experiment will indicate a potential molecular mechanism for nucleolar exclusion.

1. The authors could consider utilizing this opportunity to discuss their technological innovations in the context of the prior work of Onischenko et al., 2020. This work is referenced for the statement "RITE can be used to distinguish between old and new NPCs" Page 2, Line 43. However, it is not referenced for the statement "We constructed a RITE-cassette that allows the switch from a GFP-labelled protein to a new protein that is not fluorescently labelled (RITE(GFP-to-dark))" despite Onischenko et al., 2020 having already constructed a RITE-cassette for the GFP-to-dark transition. The authors could consider taking this opportunity to instead focus on their innovative approach to apply this technology to decrease the number of fluorescently-tagged NPCs by dilution across multiple cell divisions and to interpret this finding as a measure of the stability of nuclear pore proteins within the broader NPC.

We apologize for this imprecise citation. We have modified the text to indicate that our RITE cassette was previously used in two publications. It now reads: “We used a RITE-cassette that allows the switch from a GFP-labelled protein to a new protein that is not fluorescently labelled (RITE(GFP-to-dark)) (Onischenko et al., 2020, Kralt et al., 2022). “

1. The authors could also consider taking this opportunity to discuss their results in the context of the Saccharomyces cerevisiae nuclear pore complex structures published e.g. in Kim et al., 2018, Akey et al., 2022, Akey et al., 2023 in which the arrangement of proteins in the nuclear basket is presented, and also work from the Kohler lab (Mészáros et al., 2015) on how the basket proteins are anchored to the NPC. There is additional literature that also might help provide some perspective to the findings in the current manuscript, such as the observation that a lesser amount of Mlp2 to Mlp1 observed is consistent with prior work (e.g. Kim et al., 2018) and that intranuclear Mlp1 foci are also formed after Mlp1 overexpression (Strambio-de-Castillia et al., 1999).

Following the reviewer’s suggestion, we extended our discussion of basket Nup stoichiometry and organization in the discussion section including several of the citations mentioned. At this point, we did not see a good way to incorporate discussion about the nuclear Mlp1 foci formed after Mlp1 overexpression. However, this observation is in line with the foci formed in cells lacking Nup60, suggesting that Mlp1 that cannot be incorporated into NPCs forms nuclear foci.

Minor Points 1. What is the "lag time" of the doRITE switching? Do the authors believe that it is comparable to the approximate 1-hour timeframe following beta-estradiol induction as shown previously in Chen et al. Nucleic Acids Research, Volume 28, Issue 24, 15 December 2000, Page e108, https://doi.org/10.1093/nar/28.24.e108

Our data (e.g. newRITE, Figure S3B) suggest that the switch occurs on a similar timeframe at

1. The authors could consider a brief explanation of radial position (um) for the benefit of the reader, in Figures 1E (right panel) and 2B (right panel), perhaps using a diagram to make it easier to understand the X-axis (um).

To address this, we have now included a diagram and refer to it in the figure legend.

1. In Figure 1G, would the authors consider changing the vertical axis title and the figure legend wording from "mean number of NPCs per cell" to "mean labeled NPC # per cell" to reflect that what is being characterized are the remaining GFP-bearing NPCs over time?

Thank you for spotting this inaccuracy. We have changed the label to “mean # of labeled NPCs per cell”.

1. In Figure 2C, the magenta-labeled protein in the micrographs is not described in the figure or the legend.

As requested, a description has been added in figure and legend.

1. In Figure S2A, there is an arrow indicating a Nup159 focus, but this is not described in the figure legend, as is done in Figure 2C.

A description has been added to the legend.

1. In Figure S3C, the figure legend does not match the figure. Was this supposed to be designed like Figure 3C and is missing part of the figure? Or is the legend a typographical error?

We apologize for this error and thank the reviewer for spotting it. The legend has been corrected.

1. In Figure S4B, the spontaneously recombined RITE (GFP-to-dark) Nup133-V5 appears in the western blot as equally abundant to pre-recombined Nup133-V5-GFP. In the figure legend, this is explained as cells grown in synthetic media without selection to eliminate cells that have lost their resistance marker from the population. In Cheng et al. Nucleic Acids Res. 2000 Dec 15; 28(24): e108, Cre-EBD was not active in the absence of B-estradiol, despite galactose-induced Cre-EBD overexpression. Would the authors be able to comment further on the Cre-Lox RITE system in the manuscript?

We note that also in the cited publication, cells are grown in the presence of selection to select (as stated in this publication) “against pre-excision events that occur because of low but measurable basal expression of the recombinase”. Although the authors report that spontaneous recombination is reduced with the b-estradiol inducible system (compared to pGAL expression control of the recombinase only), they show negligible spontaneous recombination only within a two-hour time window. Indeed, we also observe low levels of uninduced recombination on a short timeframe, but occasional events can become significant in longer incubation times (e.g. overnight growth) in the absence of selection. It should be noted that in our system, Cre expression is continuously high (TDH3-promoter) and not controlled by an inducible GAL promoter. We have added the information about the promoter controlling Cre-expression in the methods section.

1. In Figure 6, the authors may want to consider inverting the flow of the cartoon model to start from the wild type condition and apply the deletion mutations at each step to "arrive" at the mutant conditions, rather than starting with mutant conditions and "adding back" proteins.

Following the suggestions of the reviewer, we have modified our model to more clearly represent the contributions of the different basket components.

Reviewer #1 (Significance (Required)):

Recent work has drawn attention to the fact that not all NPCs are structurally or functionally the same, even within a single cell. In this light, the work here from Zsok et al. is an important demonstration of the kind of methodologies that can shed light on the stability and functions of different subpopulations of NPCs. Altogether, these data are used to support an interesting and topical model for Nup2 and nuclear-basket driven retention of NPCs in non-nucleolar regions of the nuclear envelope.

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

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

In this study, Zsok et al. develop innovative methods to examine the dynamics of individual nuclear pore complexes (NPCs) at the nuclear envelope of budding yeast. The underlying premise is that with the emergence of biochemically distinct NPCs that co-exist in the same cell, there is a need to develop tools to functionally isolate and study them. For example, there is a pool of NPCs that lack the nuclear basket over the nucleolus. Although the nature of this exclusion has been investigated in the past, the authors take advantage of a modification of recombination induced tag exchange (RITE), the slow turnover of scaffold nups, the closed mitosis of budding yeast, and extensive high quality time lapse microscopy to ultimately monitor the dynamics of individual NPCs over the nucleolus. By leveraging genetic knockout approaches and auxin-induced degradation with sophisticated quantitative and rigorous analyses, the authors conclude that there may be two mechanisms dependent on nuclear basket proteins that impact nucleolar exclusion. They also incorporate some computational simulations to help support their conclusions. Overall, the data are of the highest quality and are rigorously quantified, the manuscript is well written, accessible, and scholarly - the conclusions are thus on solid footing.

We thank the reviewer for this assessment.

Reviewer #2 (Significance (Required)):

I have no concerns about the data or the conclusions in this manuscript. However, the significance is not overly clear as there is no major conceptual advance put forward, nor is there any new function suggested for the NPCs over nucleoli. As NPCs are immobile in metazoans, the significance may also be limited to a specialized audience.

We respectfully disagree with this assessment. It is becoming increasingly clear that NPC variants are also present in other model systems. We characterize the interaction between conserved nuclear components, the NPC, the nucleolus and chromatin. While the specific architecture of the nucleus varies between species, many of these interactions are conserved. For example, Nup50, the homologue of Nup2, interacts with chromatin also in other systems including mammalian cells and thus may contribute to regulating the interplay between the nuclear basket and adjoining chromatin. Furthermore, our work demonstrates the use of a novel approach in the application of RITE that can be useful for other researchers in the field of NPC biology and beyond. For example, doRITE could be applied to study the properties of aged NPCs in the context of young cells. In the revised manuscript, we attempt to better highlight and discuss the conceptual advances of our manuscript.

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

The manuscript of Zsok et al. describes the role of nuclear basket proteins in the distribution and mobility of nuclear pore complexes in budding yeast. In particular, the authors showed that the doRITE approach can be used for the analysis of stable and dynamically associated NUPs. Moreover, it can distinguish individual NUPs and follow the inheritance of individual NPCs from mother to daughter cells. The author's findings highlight that Mlp1, Mlp2, and Pml39 are stably associated with the nuclear pore; deletion of Mlp1-Mlp2 and Nup60 leads to the higher NPC density in the nucleolar territory; and NPCs exhibit increased mobility in the absence of the nuclear basket components.

The manuscript contains most figures supporting the data, and data supports the conclusions. However, authors need to include better explanations for figures in the text and figure legends. Lack of detailed explanation can pose challenges for non-experts. In addition, the authors jump over figures and shuffle them through the manuscript, which disrupts the flow and coherence of the manuscript.

We thank the reviewer for pointing this out. We have modified the figure legends throughout the manuscript in an attempt to make them more accessible to the reader. In addition, we will revise the figure order and text as suggested to improve the flow of the manuscript.

Major comments: 1) The nuclear basket contains Nup1, Nup2, Nup60, Mlp1, and Mlp2 in yeast. Nup60 works as a seed for Mlp1/Mlp2 and Nup2 recruitment and plays a key role in the assembly of nuclear pore basket scaffold (PMID: 35148185). Logically, the authors focused primarily on Nup60 in the current manuscript. However, NUP153 has another ortholog of yeast - Nup1, which has not been studied in this work. I recommend adjusting the title of the manuscript to: Nup60 and Mlp1/Mlp2 regulate the distribution and mobility of nuclear pore complexes in budding yeast. I also suggest discussing why work on Nup1 was not included/performed in the manuscript.

We have changed the title to “Nuclear basket proteins regulate the distribution and mobility of nuclear pore complexes in budding yeast”. We think that this better captures the essence of our manuscript than listing all four proteins (Mlp1/2, Nup60 and Nup2) in the title.

We initially focused on the network that is involved in Mlp1/2 interaction at the NPC. However, we agree that it would be interesting to test, whether Nup1 plays a role in the analyzed processes as well. Since Nup1 is essential in our yeast background, we will use auxin-inducible degradation of Nup1 to test its involvement in NPC distribution.

2) Figure 2B: I suggest choosing a more representative image for Pml39. It looks not like a stable component but rather dynamic as NUP60 or Gle1 based on figure showed in Figure 2B.

Due to its lower copy number, Pml39 is much more difficult to visualize than the other Nups. To guide the reader, we have now added arrow heads to point to remaining Pml39 foci at the 14 hour timepoint. The 11 hour time point most clearly show that Pml39 is less dynamic than other Nups such as Nup116, Nup60 or Gle1. At this time point, clear dots for Pml39 can be detected, while e.g. Nup116 in the same figure exhibits a more distributed signal and the signal for Nup60 and Gle1 is no longer visible. We will describe this more clearly in our revised manuscript as well.

3) Depletion of AID-tagged proteins needs to be supported by Western blot analysis with protein-specific antibodies, and PCR results should be included in supplementary data to demonstrate the homozygosity of the strains.

The correct genomic tagging of the depleted proteins by AID was confirmed by PCR. We will include this PCR analysis in the supplemental data. Please note that we are working with haploid yeast cells. Therefore, all strains only carry a single copy of the genes. Unfortunately, we do not have protein-specific antibodies against the depleted proteins. However, the Mlp1-mislocalization phenotype demonstrates that depletion of Nup60 is successful and the depletion strain for PolII depletion was used and characterized previously (PMID: 31753862, PMID: 36220102).

4) Figure 5B: Snapshots of images from the movie are required. There are no images, only quantifications.

We have replaced the supplemental movie with a movie showing the detection by Trackmate as well as overlaid tracks. As requested, a snapshot of this movie was inserted in figure 5B. We have also moved the example tracks from the supplement to the main figure. Furthermore, we will deposit the tracking dataset in the ETH Research Collection to make it available to the community.

5) Description of figure legends is more technical than supporting/explaining the figure. For example, below my suggestions for Figure 1D. Please, consider more detailed explanation for other figures. (D) Left: Schematic of the RITE cassette. NUP of interest is tagged with V5 tag and eGFP fluorescent protein where LoxP sites flank eGFP. Before the beta-estradiol-induced recombination, the old NPCs are marked with eGFP signal, whereas new NPCs lack an eGFP signal after the recombination. ORF: open reading frame; V5: V5-tag; loxP: loxP recombination site; eGFP: enhanced green fluorescent protein. Right: doRITE assay schematic of stable or dynamic Nup behavior over cell divisions in yeast after the recombination.

We have modified the figure legends throughout the manuscript to make them more explanatory and helpful for the reader.

In addition, I recommend highlighting the result in the title of the figures. Please, re-consider titles for Figure S3.

We have revised the title for Figure S3 to state a result. It now reads: “Mlp1 truncations localize preferentially to non-nucleolar NPCs.”

Minor: i) P.1 Line 31. Extra period symbol before the "(Figure 1A)".

Fixed

ii) P.2 Line 10. Inconsistent writing of PML39 and MLP1. Both genes are capitalized. The same for P.4 Line 16. In some cases all letters are capitalized in other only the first one.

We are following the official yeast gene nomenclature by spelling gene names in italicized capitals and protein names with only the first letter capitalized. We are sorry that this can be confusing for readers more familiar with other model systems but we adhere to the accepted yeast nomenclature standards.

iii) P.2 Line 18-22. The sentence is too long and hard to read. I recommend splitting it into two sentences.

We agree and have fixed this.

iv) P.2-3 Line 46-47. The sentence is unclear. Suggestion: We expected that successive cell divisions would dilute the signal of labelled and stably associated with the NPC nucleoporins. By contrast, ...

We have modified the sentence to read: “When tagging a Nup that stably associates with the NPC, we expected that successive cell divisions would dilute labelled NPCs by inheritance to both mother and daughter cells leading to a low density of labelled NPCs. By contrast,…”

v) P.4 Line 17-21. Please, consider adding extra information and clarifying lines 19-21. For example, in Line 19 Figure 2B you can add that the reader needs to compare row 1 and row 4.

Thank you, we have fixed this as suggested.

vi) P. 5 Line 15. When a number begins a sentence, that number should always be spelled out. You can pe-phrase the sentence to avoid it. Also, I recommend adding an explanation/hypothesis of why new NPCs are less frequently detected in nucleolar territory.

We have formatted the text. Interestingly, new NPCs are more frequently detected in the nucleolar territory. We have reformulated this section to make it clearer, also in response to the next comment.

vii) P.5 Line 17-22. I recommend re-phrasing these two sentences. Logically, it is clear that Mlp1/Mlp2 loss mimics "old NPCs" to look more like "new NPCs", and for that reason, they are more frequently included in the nucleolar territory, but it is not clear when you read these two sentences from the first time.

We have reformulated this section to make it clearer.

viii) P6. Line 16. No figure supporting data on graph (Figure 3B).

We have added fluorescent images of the nup2d strain to figure 4A.

ix) P.7 Line 10-13. The sentence is unclear.

We have shortened the sentence and moved part of the content to the discussion in the next paragraph.

x) P.13,14 etc. If 0h timepoint has been used for normalization, why is it present on the graph?

The 0h timepoint is shown for comparison and to illustrate the standard deviation in the data.

xi) P.15. Line 32-33. There is no image here. Potentially wrong description of the figure.

Thank you for spotting this. This was fixed.

xii) Figures: - Inconsistent labeling of figures. For example, Fig.1, Fig.1S, Figure 2 etc.

Thank you, this has been corrected.

• Inconsistent labeling of figures. For example, Fig.1 G "mean number of NPCs per cell" - no capitalization of the first letter. Fig.1S "Fraction in population" is capitalize d. In general, titles of axis should be capitalized.

Thank you for spotting this. This was fixed.

Suggestions for Figure 1D and Figure 6 are attached as a separate file.

We thank the reviewer for their suggestions to improve these figures. We have taken their recommendation and revised the figures accordingly (see also response to reviewer 1, minor point 8).

Reviewer #3 (Significance (Required)):

Zsok et al. used the recombination-induced tag exchange (RITE) approach, which is an interesting and powerful method to follow individual NUPs over time with respect to their localization and abundance. This approach has been used before in PMID: 36515990 to distinguish pre-existing and newly synthesized Nup2 populations and has been extended to other basket NUPs in this work. Using this method, the authors support the earlier data on basket nucleoporins and highlight new insights on how basket nucleoporins regulate NPCs distribution and mobility. Overall, the manuscript provides new details on the stability of nucleoporins in yeast and how these data align with the mass spectrometry and FRAP data performed earlier in other studies. The limitation of this study is the absence of data on Nup1. It was unclear why these data were not present. Additional data can be included on the dynamics of Pml39, for example, using the FRAP method. The dynamic of Pml39 at the pore was shown only using the doRITE method.

As suggested, we propose to test whether Nup1 influences NPC organization (see also above). Unfortunately, we are not able to provide orthologous data for the dynamics of Pml39. As we have discussed in the manuscript, FRAP is not suitable for the analysis of the dynamics of most nucleoporins in yeast due to the high lateral mobility of NPCs in the nuclear envelope and has previously generated misleading results for Mlp1. Furthermore, the low expression levels of Pml39 will make it difficult to obtain reliable FRAP curves for this protein. We therefore do not think that adding FRAP experiments with Pml39 will provide valuable insight.

However, in addition to the Pml39 doRITE result itself, our observation that the Pml39-dependent pool of Mlp1 exhibits stable association with the NPC supports the interpretation of Pml39 as a stable protein as well.

In general, this study represents a unique research study of basic research on nuclear pore proteins that will be of general interest to the nuclear transport field.

Field of expertise: nuclear-cytoplasmic transport, nuclear pore, inducible protein degradation. I do not have sufficient expertise in ExTrack.

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Referee #3

Evidence, reproducibility and clarity

The manuscript of Zsok et al. describes the role of nuclear basket proteins in the distribution and mobility of nuclear pore complexes in budding yeast. In particular, the authors showed that the doRITE approach can be used for the analysis of stable and dynamically associated NUPs. Moreover, it can distinguish individual NUPs and follow the inheritance of individual NPCs from mother to daughter cells. The author's findings highlight that Mlp1, Mlp2, and Pml39 are stably associated with the nuclear pore; deletion of Mlp1-Mlp2 and Nup60 leads to the higher NPC density in the nucleolar territory; and NPCs exhibit increased mobility in the absence of the nuclear basket components.

The manuscript contains most figures supporting the data, and data supports the conclusions. However, authors need to include better explanations for figures in the text and figure legends. Lack of detailed explanation can pose challenges for non-experts. In addition, the authors jump over figures and shuffle them through the manuscript, which disrupts the flow and coherence of the manuscript.

Major comments:

• The nuclear basket contains Nup1, Nup2, Nup60, Mlp1, and Mlp2 in yeast. Nup60 works as a seed for Mlp1/Mlp2 and Nup2 recruitment and plays a key role in the assembly of nuclear pore basket scaffold (PMID: 35148185). Logically, the authors focused primarily on Nup60 in the current manuscript. However, NUP153 has another ortholog of yeast - Nup1, which has not been studied in this work. I recommend adjusting the title of the manuscript to: Nup60 and Mlp1/Mlp2 regulate the distribution and mobility of nuclear pore complexes in budding yeast. I also suggest discussing why work on Nup1 was not included/performed in the manuscript.
• Figure 2B: I suggest choosing a more representative image for Pml39. It looks not like a stable component but rather dynamic as NUP60 or Gle1 based on figure showed in Figure 2B.
• Depletion of AID-tagged proteins needs to be supported by Western blot analysis with protein-specific antibodies, and PCR results should be included in supplementary data to demonstrate the homozygosity of the strains.
• Figure 5B: Snapshots of images from the movie are required. There are no images, only quantifications.
• Description of figure legends is more technical than supporting/explaining the figure. For example, below my suggestions for Figure 1D. Please, consider more detailed explanation for other figures. (D) Left: Schematic of the RITE cassette. NUP of interest is tagged with V5 tag and eGFP fluorescent protein where LoxP sites flank eGFP. Before the beta-estradiol-induced recombination, the old NPCs are marked with eGFP signal, whereas new NPCs lack an eGFP signal after the recombination. ORF: open reading frame; V5: V5-tag; loxP: loxP recombination site; eGFP: enhanced green fluorescent protein. Right: doRITE assay schematic of stable or dynamic Nup behavior over cell divisions in yeast after the recombination.

In addition, I recommend highlighting the result in the title of the figures. Please, re-consider titles for Figure S3.

Minor:

P.1 Line 31. Extra period symbol before the "(Figure 1A)".

P.2 Line 10. Inconsistent writing of PML39 and MLP1. Both genes are capitalized. The same for P.4 Line 16. In some cases all letters are capitalized in other only the first one.

P.2 Line 18-22. The sentence is too long and hard to read. I recommend splitting it into two sentences.

P.2-3 Line 46-47. The sentence is unclear. Suggestion: We expected that successive cell divisions would dilute the signal of labelled and stably associated with the NPC nucleoporins. By contrast, ...

P.4 Line 17-21. Please, consider adding extra information and clarifying lines 19-21. For example, in Line 19 Figure 2B you can add that the reader needs to compare row 1 and row 4.

P. 5 Line 15. When a number begins a sentence, that number should always be spelled out. You can pe-phrase the sentence to avoid it. Also, I recommend adding an explanation/hypothesis of why new NPCs are less frequently detected in nucleolar territory.

P.5 Line 17-22. I recommend re-phrasing these two sentences. Logically, it is clear that Mlp1/Mlp2 loss mimics "old NPCs" to look more like "new NPCs", and for that reason, they are more frequently included in the nucleolar territory, but it is not clear when you read these two sentences from the first time.

P6. Line 16. No figure supporting data on graph (Figure 3B).

P.7 Line 10-13. The sentence is unclear.

P.13,14 etc. If 0h timepoint has been used for normalization, why is it present on the graph?

P.15. Line 32-33. There is no image here. Potentially wrong description of the figure.

Figures:

• Inconsistent labeling of figures. For example, Fig.1, Fig.1S, Figure 2 etc.
• Inconsistent labeling of figures. For example, Fig.1 G "mean number of NPCs per cell" - no capitalization of the first letter. Fig.1S "Fraction in population" is capitalized. In general, titles of axis should be capitalized.

Suggestions for Figure 1D and Figure 6 are attached as a separate file.

Significance

Zsok et al. used the recombination-induced tag exchange (RITE) approach, which is an interesting and powerful method to follow individual NUPs over time with respect to their localization and abundance. This approach has been used before in PMID: 36515990 to distinguish pre-existing and newly synthesized Nup2 populations and has been extended to other basket NUPs in this work. Using this method, the authors support the earlier data on basket nucleoporins and highlight new insights on how basket nucleoporins regulate NPCs distribution and mobility. Overall, the manuscript provides new details on the stability of nucleoporins in yeast and how these data align with the mass spectrometry and FRAP data performed earlier in other studies. The limitation of this study is the absence of data on Nup1. It was unclear why these data were not present. Additional data can be included on the dynamics of Pml39, for example, using the FRAP method. The dynamic of Pml39 at the pore was shown only using the doRITE method.

In general, this study represents a unique research study of basic research on nuclear pore proteins that will be of general interest to the nuclear transport field.

Field of expertise: nuclear-cytoplasmic transport, nuclear pore, inducible protein degradation. I do not have sufficient expertise in ExTrack.