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Referee #3

Evidence, reproducibility and clarity

In the article, "The negative regulator DLK1 is transcriptionally regulated by TIS7 (IFRD1) and translationally by its orthologue SKMc15 (IFRD2)", the authors performed a double knockout (dKO) of TIS7 and its orthologue SKMc15 in mice and could show that those dKO mice had less adipose tissue compared to wild-type (WT) mice and were resistant to a high fat-diet induced obesity. The study takes advantage of number of different methods and approaches and combines both in vivo and in vitro work. However, some more detailed analysis and clarifications would be needed to fully justify some of the statements. Including the role of TIS7 as a transcriptional regulator of DLK1, SKMc15 as translational regulator of DLK1 and overall contribution of DLK1 in the observed differentiation defects. The observed results could still be explained by many indirect effects caused by the knock-outs and more direct functional connections between the studied molecules would be needed. Moreover, some assays appear to be missing biological replicates and statistical analysis. Please see below for more detailed comments:

Major comments:

-Are the key conclusions convincing? Yes.

-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? Yes. Please see my comments.

-Are the suggested experiments realistic in terms of time and resources? Recombinant DLK1 10 μg - Tetu-bio - 112€ ; 8 days of adipocyte differentiation in 3 biological replicate ~ 1 month.

-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? Adequately reproduced yes. Please see my comments concerning the statistical analysis.

1)Fig1a: In the method section it is written that an unpaired 2-tailed Student's t test was used for all statistical comparisons. However, here something like Multivariate analysis of variance (MANOVA) should rather be used to assess statistical significance between the mice. Moreover, the details of this should be clearly stated in the corresponding Figure legend.

2)Fig2a: please use an appropriate title for Fig2a instead of "Abdominal fat vs. body mass".

3)Fig2c: in the method section it is written that an unpaired 2-tailed Student's t test was used for all statistical comparisons. However, in Fig2c 4 groups are compared (WT, TIS7 KO, SKMc15 KO and dKO) and thus something like Multivariate analysis of variance (MANOVA) should rather be used to assess statistical significance.

4)Fig2 conclusion: Additive or just showing stronger effect?

5)Fig3a: the microscope picture for SKMc15 KO shows that cells might have died. Please state the percentage of cell death.

6)Fig3b: It would be informative to additionally observe some of marker genes for adipogenesis and whether all of them are affected.

7)Fig3b: instead of using an unpaired 2-tailed Student's t test with proportion, an one-way ANOVA would be more appropriate.

8)Fig3c: Same comment as for Fig3b.

9)Fig3d: A representative Western blot for 3 independent experiments is shown. Please add the other two as supplementary materials.

10)Fig3d:Is this distinguishing between the active and inactive catenin?

11)Fig4a: Please perform qPCR for measuring DLK-1 mRNA levels in TIS7 KO and SKMc15 KO samples to check whether there is a correlation between mRNA and protein level as the statement of the authors is that "DLK1 is transcriptionally regulated by TIS7 (IFRD1) and translationally by its orthologue SKMc15".

12)Fig4c: please add the other two western blots as supplementary materials.

13)Fig4d: The effects in MEFs appear quite modest. What about a rescue with TIS7 or SKMc15 alone?

14)Page 12, row 207: I would not call histones transcription factors.

15)Fig4e: Would be good to see a schematic overview of the locations of the ChIP primers in relation to the known binding sites and the gene (TSS, gene body). Moreover, the results include an enrichment for only one region while in the text two different regions are discussed. Importantly, to confirm the specificity of the observed enrichment, a primer pair targeting an unspecific control region not bound by the proteins should be included.

16)Fig5a: Has this experiment been replicated? That is no mention about the reproducibility or quantification of this result. This is the main experiment regarding the role of SKMc15 as a translational regulator of DLK1, also mentioned in the title of the manuscript.

17)Fig5b: Showing another unaffected secreted protein would be an appropriate control here.

18)Fig5c: I would recommend to perform additional experiments to prove that DLK-1 secreted in the medium can contribute and is responsible for the inhibition of the differentiation. Indeed, a time course of adipocyte differentiation followed by the addition of soluble DLK-1 would confirm that DLK-1 can inhibit adipocyte differentiation in this experimental setup. Moreover, silencing (for example RNAi) of DLK1 in the dKO cells before harvesting the conditioned media would allow to estimate the contribution of DLK1 to the observed inhibition of differentiation by the media. This is important because many other molecules could also be mediating this inhibition.

19)Fig5c: The details and the timeline of the experiment with conditioned media are not provided in the figure or in the methods. At what time point was conditioned media changed? How long were the cells kept in conditioned media? How does this compare to the regular media change intervals? Could the lower differentiation capacity relate to turnover of the differentiation inducing compounds in the media due to longer period between media change? Moreover, is the result statistically significant after replication?

20)Fig5d: please add a statistical analysis of the oil-re3d-o quantification.

21)Fig7c-d: Does overexpression also rescue the PPARg and CEBPa induction during differentiation. The importance of their induction in undifferentiated MEFs is a little difficult to judge.

22)Fig8: it is not surprising that PPARg targets are not induced in the absence of PPARg. What is the upstream event explaining this defect? Is DLK1 alone enough to explain the results? Could there be additional mediators of the differences? How big are transcriptome-wide differences between WT MEFs and dKO MEFs?

Minor comments:

1)Please use the same font in the main text for the references.

Significance

The study provides interesting insights into the role of these factors in adipocyte differentiation that would be relevant especially to researchers working on adipogenesis and cellular differentiation in general. The authors find the studied factors to have additive contribution to the differentiation efficiency. However, the exact nature of the roles and whether they are strictly speaking additive or synergistic is not clear. More detailed analysis of their contribution and molecular interplay would add to the broader interest of the study on molecular networks controlling cellular differentiation.

Referees cross-commenting

I very much agree on the different points raised by the other reviewers, some of which are also matching my own already raised concerns. And therefore it makes sense to request these modifications from the authors.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In the current study, Vietor et al. aimed to explore the regulation of Delta-like homolog 1 (DLK-1), an inhibitor of adipogenesis, and demonstrated a role for TIS7 and its orthologue SKMc15 in the regulation of adipogenesis by controlling the level of DLK-1. Using mouse models with whole body deficiency of TIS7 (TIS7 KO) or SKMc15 (SKMc15KO) and double KO (TIS7 and SKMc15 dKO) mice, the authors used a combination of in-vivo experiments and cell culture experiments with mouse embryonic fibroblasts derived from the KO animals, to show that the concurrent depletion of TIS7 and SKMc15 dramatically reduced the amount of adipose tissues and protected against diet-induced obesity in mice, which was associated with defective adipogenesis in vitro.

Major Comments:

Overall, this study presents convincing evidence that TIOS7 and SKMc15 are necessary for optimal adipogenesis, and proposes a novel mechanism for the control of DLK1 abundance via coordinated regulation of DLK-1 transcription and translation. However, a number of questions remain largely unanswered. In particular, the direct ability of SKMc15 to regulate the translation of DLK-1 is lacking, and this claim remains speculative. SKMc15 being a general inhibitor of translation, SKMc15 may have an effect on adipogenesis independently of its regulation of DLK-1. Thus, addressing the following comments would further improve the quality of the manuscript:

•The experimental evidence supporting that SKMc15 controls DLK-1 protein levels comes primarily from the observations that DLK-1 abundance is further increased in SKMc15 KO and dKO WAT than in TIS7KO WAT (Fig 3d), and that translation is generally increased in SKMc15 KO and dKO cells (Fig 5a). However, since the rescue experiment is performed in dKO cells, by restoring both TIS7 and SKMc15 together, it is impossible to disentangle the effects on DLK-1 transcription, DLK-1 translation and on adipogenesis. A more detailed description of the TIS7 and SKM15c single KO cells, with or without re-expression of TIS7 and SKMc15 individually, at the level of DLK-1 mRNA expression and DLK-1 protein abundance would be necessary. In addition, polyribosome fractioning followed by qPCR for DLK-1 in each fraction, and by comparison with DLK-1 global expression in control and SKMc15 KO cells, would reveal the efficiency of translation for DLK-1 specifically, and directly prove a translational control of DLK-1 by SKMc15. Alternatively, showing that DLK-1 is among the proteins newly translated in SKMc15 KO cells (Fig. 5a) would be helpful.

•While the scope of the study focuses on the molecular control of adipogenesis by TIS7 and SKMc15 via the regulation of DLK-1, basic elements of the metabolic characterization of the KO animals providing the basis for this study would be useful. Since the difference in body weight between WT and dKO animals is already apparent 1 week after birth (Fig 1a), it would be interesting to determine whether the fat mass is decreased at an earlier age than 6 months (Fig 1b). The dKO mice are leaner despite identical food intake, activity and RER (Sup Fig 1). It remains unclear whether defective fat mass expansion is a result or consequence of this phenotype. Is the excess energy stored ectopically? The authors mention defective lipid absorption, however, these data are not presented in the manuscript. It would be interesting to investigate the relative contribution of calorie intake and adipose lipid storage capacity in the resistance to diet-induced obesity. In addition, data reported in Fig 1c seem to indicate a preferential defect in visceral fat development, as compared to subcutaneous fat. It would be relevant if the authors could quantify it and comment on it. Are TIS7 and SKMc15 differentially expressed in various adipose depots? The authors used embryonic fibroblasts as a paradigm to study adipogenesis. It would be important to investigate, especially in light of the former comment, whether pre-adipocytes from subcutaneous and visceral stroma-vascular fractions present similar defects in adipogenesis.

We estimate the suggested experiments above realistic in terms of time and resources and important to support the major conclusions of the study. Both data and methods are explained clearly. The experiments are, for the most part, adequately replicated. However, whenever multiple groups are compared, ANOVA should be employed instead of t-test for statistical analysis.

Minor comments:

•Figure 4 d. The appropriate control would be WT with empty vector

•Figure 7c/d. The appropriate control would be WT with empty vector

•Figure 5C. An additional control would be WT with WT medium

•Figure 2: In the legends, the "x" is missing for the dKO regression formula

•Since the role of SKMc15 in adipogenesis has never been described, the authors could consider describing the single SKMc15 KO in addition to the dKO, or explain the rationale for focusing the study on dKO.

Significance

While the effects of DLK-1 on adipogenesis have been widely documented, the factors controlling DLK-1 expression and function remain poorly understood. Here the authors propose a novel mechanism for the regulation of DLK-1, and how it affects adipocyte differentiation. This study should therefore be of interest for researchers interested in the molecular control of adipogenesis and cell differentiation in general. Furthermore, the characterization of the function of SKMc15 in the control of translation may be of interest to a broader readership.

Referees cross-commenting

I agree with all the comments raised by the other reviewers. Addressing the often overlapping but also complementary questions would help to clarify the molecular mechanisms by which TIS7 and SKMc15 control adipogenesis, and support the conclusions raised by the authors.

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Referee #1

Evidence, reproducibility and clarity

This study by Viedor et al. examines the role of TIS7 (IFRD1) and its ortholog SKMc15 (IFRD2) in the regulation of adipogenesis via their ability to modulate the levels of DLK1 (Pref-1), a well-known inhibitor of adipogenesis. They generate SKMc15 KO mice and cross them to previously published TIS7 KO mice. All 3 mutant strains show decreased fat mass, with the effect being most pronounced in double KO mice (dKO). Using mouse embryonic fibroblasts (MEFs) from mutant mice, they authors ascribe a defect in adipogenic differentiation of mutant cells to an upregulation of DLK-1. In the case of TIS7, they propose that this is due to its known inhibition of Wnt signaling, which regulates DLK-1 expression. In the case of SKMc15, they suggest a new mechanism linked to its ability to suppress translation. Overall, the work is of interest, with the finding that SKMc15 regulates adipocyte differentiation being its novelty, and generally well done, though multiple aspects need to be improved to bolster the conclusions put forth.

Major concerns:

1)The main mechanism put forth by the authors to explain the inability of dKO cells to differentiate into adipocytes is the upregulation of DLK-1 levels. However, this notion is never directly tested. Authors should test if knockdown of DLK-1 in dKO cells is sufficient to correct the defect in differentiation, or if additional factors are involved.

2)There are multiple instances were the authors refer to "data not shown", such as when discussing the body length of dKO mice. Please show the data in all cases (Supplementary Info is fine) or remove any discussion of data that is not shown and cannot be evaluated.

3)Indirect calorimetry data shown in Fig. S1 should include an entire 24 hr cycle and plots of VO2, activity and other measured parameters shown (only RER and food intake are shown), not just alluded to in the legend.

4)It is surprising that the dKO mice weight so much less than WT even though their food consumption and activity levels are similar, and their RER does not indicate a switch in fuel preference. An explanation could be altered lipid absorption. The authors indicate that feces were collected. An analysis of fat content in feces (NEFAs, TG) needs to be performed to examine this possibility. The discussion alludes to it, but no data is shown.

5)It would be important to know if increased MEK/ERK signaling and SOX9 expression are seen in fat pads of mutant mice, not just on the MEF system. Similarly, what are the expression levels of PPARg and C/EBPa in WAT depots of mutant mice?

6)Analysis of Wnt signaling in Fig. 3c should also include a FOPflash control reporter vector, to demonstrate specificity. Also, data from transfection studies should be shown as mean plus/minus STD and not SEM. This also applies to all other cell-based studies (e.g., Fig. 6b,c).

7)It is unclear why the authors used the MEF model rather than adipocyte precursors derived from the stromal vascular fraction (SVF) of fat pads from mutant mice. If they did generate data from SVF progenitors, they should include it.

8)Given that the authors' proposed mechanism involves both, transcriptional and post-transcriptional regulation of DLK-1 by TIS7 and SKMc15, Fig. 4d should be a Western blot capturing both of these events, and not just quantitation of mRNA levels.

9)There is no mention of the impact on brown adipose tissue (BAT) differentiation of KO of TIS7, SKMc15, or the combination. Given the role of BAT in systemic metabolism beyond energy expenditure, the authors need to comment on this issue.

Minor comments:

10)The y axis in Fig. 2c is labeled as gain of body weight (g). Is it really the case that WT mice gained 30 g of body weight after just 3 weeks of HFD? This rate of increase seems extraordinary, and somewhat unlikely. Please re-check the accuracy of this panel.

11)The Methods indicates all statistical analysis was performed using t tests, but this is at odds with some figure legends that indicate additional tests (e.g., ANCOVA).

12)Please specify in all cases the WAT depot used for the analysis shown (e.g., Fig. 3d is just labeled as WAT, as are Fig. 4a,e, etc.).

13)Fig. 5d is missing error bars, giving the impression that this experiment was performed only once (Fig. 5c). The legend has no details. Please amend.

Significance

The role of TIS7 in adipocyte differentiation is well established. The only truly novel finding in this work is the observation that SKMc15 also plays a role in adipogenesis. The molecular mechanisms proposed (modulation of DLK-1 levels) are not novel, but make sense. However, they need to be bolstered by additional data.

Referees cross-commenting

I think we are all in agreement that the findings in this work are of interest, but that significant additional work is required to discern the mechanisms involved. In my view, a direct and specific link between SKMc15 and translation of DLK-1 needs to be established and its significance for adipogenesis in cells derived from the SVF of fat pads determined. Reviewer 2 has suggested some concrete ways to provide evidence of a direct link.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

Summary: The manuscript analyzes how the constriction of a tissue by an enveloping basement membrane alters the migration of cells migrating through that tissue. The tissue analyzed is the Drosophila egg chamber, an important model for basement membrane studies in vivo, and the cells migrating through it are the border cells. The border cells migrate through the center of the egg chamber, moving as a cluster between the nurse cells, which are in turn surrounded by follicle cells, which secrete the basement membrane on the outside of the egg chamber. The authors decrease and increase the basement membrane stiffness with various genetic perturbations, and they find that the border cells move more rapidly when the stiffness is reduced. They then investigate how basement membrane stiffness is communicated to the border cells several cell layers inside, by measuring cortical tension with laser-recoil. They found that external basement membrane stiffness alters the cortical tension of the nurse cells and the follicle cells, such that reduced matrix stiffness causes reduced cortical tension; further, reducing cortical tension directly within the cells also results in increased border cell migration rates. They conclude that basement membrane stiffness can alter cell migration in a new way, by altering constriction and cortical tension, with an inverse relationship between stiffness and migration rate. This is a strong manuscript and I would request very few changes.

The authors are commended on the rigor and completeness of their study. Several independent methods are used to alter basement membrane stiffness (loss of laminin, knock-down of laminin, knock-down of collagen IV, over-production of collagen IV - all of which end up changing collagen IV levels) and all show the same result. Further, they are extremely rigorous about testing and excluding an attractive alternative hypothesis, that the basement membrane of the border cell cluster itself controls its migration rate. The use of mirror-Gal4 is very elegant and convincing, as it expressed only in the central part of the egg chamber, and they found border cells responded differently only in that region. Moreover, the authors were exceptionally thorough in reproducing the basement membrane mechanical data in their own hands using the bursting assay. Overall, the experimental data support the claims of the paper. There is only one more control I would like to see, for the knockdown of laminin in the border cell cluster with a triple-Gal4 combination. Presumably using all three Gal4 lines was necessary to get complete knockdown, and it would be nice to see anti-laminin for the border cell cluster under these knockdown conditions.

Despite the rigor, because all of the manipulations to the basement membrane alter the levels of collagen IV, the authors cannot formally exclude the possibility that collagen IV in the basement membrane has another function besides stiffness, perhaps sequestering a signaling ligand, and that this other function somehow alters the cortical tension of the egg chamber. In the paper by Crest et al, externally applied collagenase served as a control for this possibility, but collagenase will not work for the authors because this study is in vivo. I suggest the authors bring up this caveat in the discussion. If they wanted to extend the study (optional), they could knock down the crosslinking enzyme peroxidasin in the egg chamber, which ought to reduce basement membrane stiffness without changing the collagen content. The problem here is that it hasn't already been shown to work that way in the egg chamber, and so both stiffness and collagen levels would need to be measured. Testing the stiffness directly would be difficult, since the bursting assay is not actually a measurement of stiffness (more on that below). Rather than go this route, I suggest just acknowledging the formal possibility, which seems to me unlikely anyway.

In terms of clarity, the manuscript absolutely needs a schematic at the beginning to introduce the egg chamber and border cell migration, labeling the cell types, showing the route and direction of border cell migration, and labeling the A/P axis. Without this the non-expert reader cannot readily understand the study.

Finally, in terms of clarity, the authors repeatedly use statements such as "stiffness influences migration rate". Influences how? These results are not intuitive to me, and it would help enormously if the authors would make statements like, decreasing stiffness increases migration (as I tried to in my summary). Here are two examples of statements to refine: • Line 189 - "We found that reducing laminin levels affected the migration speed of both phases (Fig.1F, G)." Please say increased, not affected. • Line 245 -"Altogether, these results demonstrate that the stiffness of the follicle BM influences dynamics and mode of BC migration." Again, be specific about how. There are many such statements, from the abstract to the results to the discussion, where it would help the clarity to be more precise about what kind of influence.

Minor comments: • The movies are beautiful! • All the quantitative data are shown in bar charts with means and errors. It is much better to show the individual data points, superimposing the means and distributions on top of the individual points. • The bursting assay does not actually measure basement membrane stiffness; rather, it measures failure after elastic expansion. These are related, as was found by Crest et al and the authors say that at one point, but stiffness and failure are not the same thing. Please change the language discussing this assay to "mechanical properties" rather than stiffness. • The laser-recoil assays are done well and are convincing. Throughout the results section, the authors describe these as measuring "cortical tension", which is correct. However, in the figure legends the language changes to "membrane tension" which is only one component of cortical tension. Change them all to cortical tension. • In the Discussion, it would be nice to include something on the two different modes of migration (tumbling and not tumbling). • I suggest changing the title to remove the word "forces", because forces are never directly measured from basement membrane. • Although Dai et al (Science 2020) is discussed near the end, I suggest bringing this reference up to the introduction, so the reader can have the background on the mechanical aspects of border cell migration at the start of this study. • Two typos (there may be more): At the bottom of Fig. 2, text turns strangely white that should probably be black; and in line 260, you mean Fig. S5 not S4 (laser ablation).

Significance

Mechanobiology, and mechanobiology of the basement membrane, is a vibrant area of study now, arising from the intersection of biophysics/engineering and genetics. There is general interest in how the basement membrane alters forces within the tissue, and this study is the first to my knowledge to relate basement membrane mechanics to migration via constriction and cortical tension. The authors do a great job of discussing the broader significance of their work in the Discussion. To greatly broaden the scope of this work in the future, the authors could collaborate with a mouse team to look for similar responses in a mammalian tissue, as they discuss. It is worth noting that there is a lot of work on matrix stiffness and migration showing that stiffness promotes migration speed; in these cases, matrix is a substrate, not a compression mechanism. But the opposite nature of the result in interesting and makes this work non-intutive and perhaps hard for some readers to grasp.<br /> As the paper is written now, I think the audience for this work would mostly be oogenesis, border cell migration, and/or basement membrane researchers in the Drosophila community, of which there are many (I am in this camp). With some rewriting to make it more accessible to other audiences, I think it would be interesting to a larger developmental biology audience. The content is not like any other paper I know, but it may be similar in scope and subject matter to the papers detailing how follicle cells and basement membrane interact during follicle rotation.

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Referee #2

Evidence, reproducibility and clarity

Ester and her colleagues described a force model that controls border cell migration by varying the stiffness of the basement membrane. It's based on the modification of laminin and Coll IV which are components of the basement membrane. To reduce BMs stiffness, they introduced LanB1RNAi or the LanB1 mutant to inhibit laminin production or vkgRNAi to reduce Coll IV. They also applied EHBP1mCh to enhance BM stiffness. Furthermore, they applied laser ablition to confirm that the BM stiffness affects the tension of nurse cells and follicle cells, thus regulating border cell behavour by changing environmental properties. It is a nice work revealing how the environment controls border cell migration; however, there are several points that concern me: 1. It's reported that actin polymerization at the front of the cell generates protrusions, as well as that myosin contractility helps to suppress lateral random protrusions, thus leading to a directed and efficient cell migration. So why do more lateral protrusions (tj>LanB1RNAi) produce a faster migration speed? 2. We know some labs also did experiments with those Kel/Dic mutant flies. And the Kel mutant is very sick, which sometimes leads to NC degeneration. As a result, we have serious doubts that this mutant's border cell migration will remain normal. 3. From figure4, we noticed that with mirrGal4, the vertex distance increase is much lower than tjGal4 (control of D, H and K), and even with expressing the EHPB1mCh, the distance is still lower than the tjGal4 control. These indicate the NC cortical tension is lower with mirrGal4 expression, which is patially against the paper's main point. (Similar issue in figure5 D and E). 4. Sfigure1 A and B seem not to have the right contrast (the blue and the red should have the same brightness), so the comparison of the intensities might be inaccurate and needs to be requantified after adjustment of the images. 5. Sfigure2 A-E showed that the vkgRNAi has the highest bursting frequency, whereas F and G do not. And the majority of the data from F does not fit with A-E, and it is unclear what timepoint sF.G. is at. 6. SFigure 6 only displayed a representative image of the control condition; the lack of representative images for the other conditions resulted in unconvincing results. 7. Some figures and movies have prominent variation of migrating stages, such as not-detached border cells compared with detached border cells. This might strongly cause the results inconsistent with each other. 8. There are numerous typos in both the manuscript and the figures. Based on all these concerns, I recommend authors to do some improvement before this manuscript is accepted by some reputed journals.

Significance

Strengths: the manuscript is well written and organised; limitation: figures and results are not supportive enough, and thus conclusion is not completely convincing, statistical quantification is not clear and somehow confusing.

Advice: If the conclusion is solid, this story will fill the unclear importance of surrounding environment on cell-rich tissue for collective cell migration. Concept is very novel while needing more supporting data. It is a fundamental study for development biology.

Audience: The story will fit well for developmental and cell biology, as well as people with biomechanical background.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Lopez et al have employed the ex vivo model of Border cell migration in Drosophila ovaries to examine the constriction forces imposed by basement membrane on migrating border cells. The authors have extensively employed live cell imaging coupled with genetics to demonstrate that basement membrane encasing fly eggs modulates the dynamics of migrating border cells. Through laser ablation experiments they show that basement influences the tension of the underlying follicle cell and nurse cells which in turn affects the migration efficiency of collectively moving border cells. Over all the experiments are well quantified with good degree of statistics that drive the claim of the authors.

Major comments: Over in all the images, it is very hard to appreciate the overall contour of the egg chamber. This is important to get an insight regarding the stage of the egg chamber being evaluated.

1. By depleting the constituents of basement membrane, the authors show that the speed of the migrating border cells increases. However in Supplementary Figure 1A and B where that authors have depleted LanB1, the migrating border cell cluster seems to lag while the control has reached the oocyte boundary. Is this a single off phenomena?

2. This is regarding the osmotic swelling experiments. The frequency and speed of bursting of egg chambers in deionized water was used to evaluate the stiffness of basement membrane in different genetic background. As egg chambers of different stages have variable sizes, it would be fair to evaluate egg chambers of only a particular stage for this analysis as the tonocity of the egg chambers may depend on their size.

3. Line 211, "Live time lapse imaging, showed that the overexpression of EHBP1mCh in all FCs delayed BC migration (tslGFP; tj> EHBP1mCh, Figure S4A-B', Movie S4, n=6)." Though the border cell cluster hasn't moved significantly in Fig S4B', the egg chamber development seems to be stalled as the movement of main body follicle cells is affected. My concern if over expression of EHBP1mCh in the follicle cells is stalling the oogenesis itself could that indirectly affect the border cell movement. Secondly though EHBP1 has been shown to affect secretion of the basement membrane constituents, it could also modulate asymmetric secretion of other components. Can the authors evaluate if over expression of EHBP1mCh rescues the delay in migrating border cells in Lanb1 heterozygous background to render stronger support to their claim.

4. In Supplementary Fig 7 B and B' the nurse cell morphology seems to be affected. Could the distorted nurse cell morphology in the abi-depleted germline cell affecting the migration efficiency of border cells.

5. Line 313-314 The authors state that "The radius of curvature of a spherical interface is inversely proportional to the difference in pressure between the two sides of the interface." This may be applicable to a smooth surface but may be not directly applicable to the cell membrane as there are local regional variations and thus any inference on the cytoplasmic pressure of nurse cells may be misleading.

Minor comment:

1. In supplementary figure 6D, the square boxes are obscuring the border cell membrane and it will be better if the authors can modify the figure to render more clarity.
2. There are couple of places where sentence structure needs to be corrected.

Referees cross-commenting

I agree with all the comments of other reviewers. Overall I also feel that results do not strongly support the main conclusions. The authors draw major conclusions based on experiments that are merely suggestive rather than being conclusive. Some of the concerns are listed. Like Reviewer 3 raising the concern that Collagen IV may have other functions in the basement membrane other than providing stiffness. A similar concern I too have raised regarding over-expression of EHBP1. I agree with Reviewer 3 that there are several other factors that can affect the outcome of bursting assay besides the stiffness of the basement membrane itself. So the authors need to be careful in linking the bursting frequency of the egg chamber with the stiffness of the basement membrane itself.

I agree with other reviewers that the quality of the images need to be better. In addition, the image presented should be representative of the population and should fit with the over claim made by the authors (Point No 3 of Reviewer 2 and Point No 1 of Reviewer1). I also agree that authors need to explain Reviewer 2's concern (Point No-1) as to why the lateral protrusion in tj>LanB1RNAi doesn't inhibit the movement of border cell clusters but rather produce faster migration speeds?

Lastly it is important for the authors to verify that like Kel/Dic mutants are indeed effective or any genetic perturbation like overexpression of EHBP1mCh is not the stalling the oogenesis progression perse, thus giving a false impression of altered migratory speed of border cell clusters.

Significance

The role basement membrane is well documented in affecting the shape of neighbouring cells Here the authors claim that the stiffness of basement membrane is regulating the migration efficiency of the border cells. I believe that basement membrane encasing the follicle and underlying germline cells provides a very narrow passage for the border cells to migrate. Any mechanical perturbation that releases or increases the pressure or make the nurse cells membranes less or more taut will affect the dynamics of migrating border cells. Though the authors have demonstrated this with very elegant experiments, I am afraid that their findings are standard outcomes in any physically constrained system and somehow doesn't significantly advance the field.

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Reply to the reviewers

Manuscript number: RC-2022-01776

Corresponding author(s): David Bryant

1. General Statements [optional]

We describe an ARF6 GTPase module that controls integrin recycling to drive invasion in PTEN-null Ovarian Cancer (OC). We used high-throughput, time-lapse imaging and machine learning to characterise spheroid behaviours from a series of cell lines modelling common genetic lesions in OC patients. We identified that PTEN loss was associated with increased invasion, the formation of invasive protrusions enriched for the PTEN substrate PI(3,4,5)P3, and enhanced recycling of integrins in an ARF6-dependent matter. We utilised Mass Spectrometry proteomics and unbiased labelling to investigate the interactome of ARF6, identifying a single ARF GAP (AGAP1) and a single ARF GEF (CYTH2). Importantly, this ARF6-AGAP1-CYTH2 modality was associated with poor clinical outcome in patients.

We thank all Reviewers for their highly complementary assessment of our manuscript, describing our paper as a "very impressive study, very well done and controlled with rigorous statistical analyses that uses sophisticated methods", a study that is "stunning in its thoroughness and depth and breadth of its molecular analysis", with "experiments are properly designed, and the data are well presented. The conclusions are appropriate and supported by the data". Finally, we would like to thank the reviewers for appreciating that our results are "of significance for both scientific discovery and clinical application, which will interest the broad audience in both basic and clinical research".

2. Description of the planned revisions

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

Reviewer comments in bold. Our response in non-bold.

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

This paper by Konstantinou et al aims at deciphering the mechanisms by which PTEN loss could be driving poorer prognosis in patients. The authors use their great high-throughput 3D screening method coupled to an unbiased proteomic method and a CRISPR screen to uncover a new pro-invasive axis driving collective invasion of high-grade serous ovarian carcinoma (HGSOC) cells. Overall, this is a very impressive study, very well done and controlled with rigorous statistical analyses that uses sophisticated methods to convincingly show that the CYTH2-ARF6-AGAP1-ITGA6/ITGB1 module is required for the pro-invasive effect of PTEN depletion and discriminates patients with poorest prognosis.

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MAJOR COMMENTS __

Below are listed all the claims that, in my opinion, are not adequately supported by the data.

1) Choice of the cell line: More justification on the use of the ID8 cell line and on the p53 deletion is needed. The authors need to clearly state that most p53 mutations in ovarian cancer are missense mutations that lead to a strong accumulation of a p53 protein devoid of transcriptional activity. Nevertheless, it seems that p53 mutations are not associated to differences in patient survival. Hence the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained. Moreover, the in vivo experiments already performed in the literature mentioned in the discussion should be mentioned in the introduction to provide more context and physiological relevance to this study (especially regarding the special focus on the p53 null/ dKO cells throughout the study).

We will update the manuscript with a detailed explanation of the cell line of choice. Briefly, while indeed Tp53 is found mutated in HGSOC, approximately 30-35 % of these are classified as null mutations (PMID: 21552211), making models with null Trp53 representative of the clinical situation. Further, there is no difference in patient outcome in HGSOC by Tp53 mutation type (PMID: 20229506), while gene expression data from TCGA suggest that HGSC is marked by loss of wild-type P53 signalling regardless of Tp53 mutation type (PMID 25109877). Thus, we believe our choice of model can faithfully mirror the clinical situation.

2) "Therefore, PTEN loss in ovarian cancer, particularly at the protein level, occurs in the tumour epithelium and is associated with upregulated AKT signalling and poor overall survival". This claim is an over-interpretation and over-generalisation of the data presented. I appreciate the honesty of the authors in showing all the ovarian datasets that are available and highlight the discrepancies in expression of the proteins they study in stroma and epithelium. I think the way to present these data in the text without over-interpreting and generalizing would be to show that there is a clear epithelial-specific downregulation of PTEN at the mRNA level. Most likely due to the contribution to other cell types in the stroma, only 3 out of 5 bulk tumour mRNA datasets show a tumour specific downregulation of PTEN and no association with survival based on a median split of PTEN mRNA expression. Nevertheless, although there is no direct correlation between PTEN mRNA and protein levels, patients with low PTEN protein levels have poorer survival that is associated to an upregulation of Akt signalling. This allows to have a clearer conclusion, based solely on the protein data presented and no over-generalisation using the mRNA data. This, to me, makes a stronger case for studying PTEN loss in ovarian cancer and is fully supported by the data presented.

We will incorporate this reviewer suggestion into the modified manuscript.

3) PTEN loss induces modest effects in 2D culture. The authors make claims regarding the fact that some of the phenotypes they look at happen after PTEN depletion alone or in combination with p53 loss and are more prominent in 3D vs 2D. Many of these are insufficiently backed up by data. A few key experiments are also only performed in 2D and should be done in 3D. Finally, some clarifications if the role of PTEN is most prominent on either collective, ECM-induced or 3D-dependent invasion.

some clarifications if the role of PTEN is most prominent on either collective, ECM-induced or 3D-dependent invasion

We believe that the reviewer may be confused. Both of our models, either spheroids or invading monolayers, are events occurring inside gels of ECM. Therefore, these are all are 3D, ECM-induced, collective invasion. We have not performed 2D migration assays. We apologise that the this was not clearer in the first submission. We will correct this in the updated manuscript.

First, the authors claim that PTEN loss alone (i.e. without p53 deletion) leads to changes in Akt signalling. Supp fig 1H clearly shows that there is no significant increase in Akt activation, although there seems to be one in the Western Blot (WB) presented in supp fig 1G. There is a clear, significant increase in the Akt activation in all the PTEN KO clones when in association with p53 loss though. This claim is hence not backed up by data and the conclusion seems to be that the effect on Akt signalling requires both deletion of p53 and PTEN.

The reviewer is correct: that the increase to pAKT levels upon PTEN KO is more robust with co-KO of TP53, thereby indicating synergy with p53. We will update the manuscript to note this, accordingly.

It will be interesting to see a quantification of the pS473-Akt staining (supp fig S1J), as it seems from these images that pAkt is preferentially found on rounded cells. It should also be performed in 3D conditions to see if there is an enrichment at invasive tips and back-up the invasion data.

This observation made us realise that the images we had included were giving the wrong impression (that pAkt levels would be highest in round cells). Based on the quantitation in Fig. S1M, PTEN KO cells (which have elevated pAkt levels), show a marked depletion of rounded cells. Therefore, pAkt elevated is not associated with being enriched in rounded cells. We will replace this image with cells mirroring the phenotypes quantified in Fig S1M.

We used 2D for quantitation of pAKT staining, as we perform a like for like comparison. We cannot compare pAkt in 3D protrusions accurately between genotypes because of the frequency of protrusions: in p53 KO protrusion are rare. In 3D, therefore, it is not a situation where protrusions are present in both genotypes and we compare enrichment or depletion in a stable structure. Rather, what we can provide is whether when protrusions form, there is clear pAkt labelling in a protrusion. We will include for the revision a representative image of each phenotype in 3D, including a 3D Trp53-/-;Pten-/- spheroid stained for pAKT S473.

Arf6 is recruited to the invasive tips of cells invading a 2D wound (fig4D). How do the authors reconcile the fact that all the machinery required for 3D invasion is present but that PTEN loss has a modest effect on cells in 2D? If the wound assay was done on glass, it should be done again on ECM coated glass to see if it recapitulates the effects seen in 3D. This experiment will help deconvolute if the effect of PTEN loss is more linked to collective behaviour than 3D organization or presence of ECM.

We again apologise for not being clearer in our description. Both the wound assays and the IF of invading monolayer were performed with cell monolayers invading into Matrigel. Monolayers are grown on top of Matrigel, wounded, and then overlayed with Matrigel. Therefore, this is orthogonal to our spheroid assay, and completely 3D. We will address this comment by changing the text in the results section to highlight the 3D nature of the method.

The recycling assays are all done in 2D, condition under which the authors claim that the PTEN phenotype is weakest. Although I understand that it is not possible to do this assay in 3D, its contribution to elucidating the mechanism by which integrins participate in the PTEN loss invasive phenotype is not clear. The requirement of integrins relies on the data showing that ITGB1 KO results in no collagen4-positive basement membrane of the cysts and greatly impaired invasion. Experiments looking at the integrin localisation would be helpful: can an enrichment at the invasive tips can be seen? Are ITGA6 and/or ITGB1 repartitions homogeneous between the cysts membranes and the invasive tips? In my opinion the Src/FAK data is not enough to draw the conclusions of fig7I schematic.

We will endeavour to include images of 3D spheroids of Trp53-/-;Pten-/- cells and stained for β1 integrin (total and active) and α5 integrin to interrogate localisation at the tips.

4) Expression of AGAP1 isoforms do not alter ARF6 levels. Data in fig 6C, D show a significant downregulation of Arf6 and Akt signalling after expression of AGAP1S. Can the authors clarify what they mean?

We thank the reviewer for picking up that discrepancy between the results and the text. We will change the relevant text to highlight that expression of AGAP1S is associated with a statistically significant reduction of roughly 30% in ARF6 levels and 10% in p:t AKT. We do not know why AGAP1s may enact such an effect.

5) Arf6 is not modulated in the different cell lines: data in fig4B (far right graph) and supp fig 4B, J seem to indicate otherwise. Can the authors clarify what they mean?

It is not clear exactly what the reviewer is referring to here. If the reviewer is referring to Supplementary Figure 4B, this is an experiment examining the levels of ARF5 or ARF6 upon knockdown, so levels would be expected to vary. Fig S4B does not correspond to the experiment performed in S4J. Our interpretation is that loss of p53 alone or in combination with Pten does not seem to be consistently be accompanied with an increase in either the levels of total or bulk GTP-bound ARF6 that could explain the dependency of Trp53-/-;Pten-/- on the GTPase for the invasive phenotype. We will make our interpretation clearer in the text

6) Immunofluorescence panels without quantifications: Quantifications for the different stainings shown in fig3A; 4D, E; 5H; 7B and supp fig S1L, J; S3 need to be included to fully back the conclusions of the authors. Indeed, these images are used to draw conclusions and not only as illustrations.

It is not possible to do a direct comparison between protrusion vs no protrusion (see our response above). We will include a line scan to show clear enrichment at the end of the tip for image shown. Quantitation for Figure S1L is already included (S1K and M), quantitation for Figure S1J is presented in Fig S1I and for Fig 5H quantitation of the phenotype is present in Fig 5I.

7) Quantifications of invasion show that WT cysts become hyper-protrusive at around the half experiment mark (around 30-40hrs). Nevertheless, all movies or galleries show spherical cysts, which does not seem representative. Can the authors change this or explain why these images/movies were chosen?

We present the fold change at each time point because that is intuitively easier to understand rather than the raw number. The quantitation does not show that the cysts necessarily become hyper-protrusive at the specific timepoint, but rather that the proportion of hyper-protrusive cysts observed in this genotype peaks at the specific timepoint. This phenotype may still be in the minority of behaviours. As an example, something that occurs 5% of the time in the control, with a two-fold increase in behaviours, might still only be 10% of the population. Therefore, adding in a picture that may be representative of a small proportion of the population may not be a realistic depiction of what is happening across the entire population. We will provide the reviewer with the exact percentage of spheroids that are classified as hyper-protrusive at the specific cell line across timepoints, to make this clearer.

8) Since it seems that the main effect of PTEN is to drive the localisation and intensity of recycling of Arf6 cargoes, it will be helpful to confirm that all the proteins involved in the Arf6 module be shown to be accumulated/present at the pro-invasive tips. Immunofluorescence stainings showing the presence of AGAP1 (could be done with the AGAP1S isoform that is mNeon-tagged), pS473-Akt, ITGB1 (active integrin if possible, otherwise total integrin), ITGA5, PI3K should be included if possible. A quantification comparing signal in the cysts and in the invasive tips should also be included to see if there is an accumulation to PIP3-enriched areas.

We will endeavour to include the requested images.

9) Data in fig5I convincingly show that PTEN loss induces a fragmented collagen4-positive basement membrane. The authors use this data to claim that this is one of the ways that PTEN could be driving invasion but no correlation between these structures and the hyper-protrusive phenotype is made. This experiment needs to be done to support this claim.

This comment made us realise that in an attempt to make images simpler (displayed nuclei and COL4 only), we omitted a staining for where protrusions were moving through gaps in the ECM. We will update these times to demonstrate such events.

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MINOR COMMENTS __

1) Data visualization: I think that the heatmap representation is overkill when only 2 or 3 conditions are presented. A graph showing the evolution of area or spherical/Hyper-protrusive phenotype proportions across time would be easier to read and more impactful: each genotype could be presented with a colour and the spherical/hyper-protrusive phenotypes as either plain or dashed lanes across time. I understand that this representation allows for the stats to be done at each time points but they are generally pretty clear (especially for the PTEN KO or dKO phenotypes) and do not need to be done for each time point in my opinion. These heatmaps could be put in supplementary figures if the authors feel strongly about putting stats for each time points.

We thank their reviewer for their suggestion. We believe that our approach, while complex, is the best visualisation to reflect both the changes across time but also between conditions while allowing appreciation of the statistical significance. This visualisation has been optimised by our lab over years of working with this type of data and we would prefer that they remain consistent with the accepted standard of our other publications. We are, however, happy to expand the explanation in the text on how to interpret the bubble heatmaps.

Fig supp S1M, fig 5I should be presented as a stacked histogram to improve readability and merged with fig supp S1K.

We will merge Figures S1M and S1K. We believe that Figure 5I is easier to read as is.

Displaying fold change as antilog rather than log values would be easier for the reader to realise the magnitude of the differences.

We disagree with the reviewer.

A bar graph would be easier to read than the matrix representation for fig 6B.

We disagree with the reviewer as we feel it makes it easier to directly compare each lipid between the two cell lines.

The way Area data is presented throughout to me makes it very difficult to understand what is going on. Could the authors at least give some explanations in figure legends. A curve graph displaying the evolution of the area across time would be easier to read and see the differences between conditions.

Please see our response to Minor point 1

2) It is confusing that, in fig supp S1M, there is a significant decrease of the rounded phenotype after PTEN loss that is not associated to a significant change in another of the categories. Could the authors explain how?

This can be simply explained from our data: while the rounded phenotype was reduced in a consistent way across replicate experiments (therefore resulting in significance), the effect on the other two phenotypes was not consistent (not set in magnitude and directionality). This therefore does not lead to a significant (i.e. consistent) effect on the latter two phenotypes. PTEN loss therefore seems to allow cells to undergo – at the expense of being round - a range of shape changes, rather than a set phenotype.

3) One of the big differences of the PTEN KO cells seems their ability to invade through the matrigel bed and migration on the glass below (supp movie S2). From what I gather, these cysts would be considered out of focus and excluded from the analysis. Would it be possible that this would minimize some of the results? Would it be possible to include a quantification of this particular phenotype to confirm it is specific to PTEN KO cells?

In the same spirit, could the authors provide the percentage of non-classified cysts, to make sure that the same proportion of cysts is quantified across all different genotypes.

Indeed, we cannot exclude that we under-estimate the magnitude of the effect on the PTEN null. We will include this point in the discussion. We can include a reviewer-only figure showing the proportion of cysts and levels of the ‘OutOfFocus’ objects across cell lines.

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4) Can the authors clarify how a 0 fold change (in log value) in fig 2D can be highly significant? __

We believe that the reviewer is equating statistical significance with something being biologically meaningful. Statistical analysis does not indicate a priori whether something is biologically meaningful. Rather, it assesses the likelihood that an observed result is occurring by chance (or not). For instance, if a small change (e.g 0.04 in a log2 fold change) occurred repeatedly across experimental replicates this is unlikely to be a result of chance, and therefore could be statistically significant. Yet, such a small magnitude of effect is probably biologically minor. This is why our heatmaps provide both statistical significance, fold change, and consistency in magnitude of effect.

5) Delta isoform of PI3K seems to have an effect on area in the middle of the experiment, but has no effect at all on invasion. Could the authors comment? Are these smaller cysts still as invasive? There might be an interesting uncoupling between proliferation and invasion there.

The cysts are actually slightly larger with PI3Kδ inhibition and there is no change in invasion. We will expand our comments in text as well to account for this observation.

6) ITGB1 depletion seems to induce a downregulation of Akt protein. Is that right? Does it change Akt localisation? Is there a dose effect whereby there is not enough Akt protein to mediate invasion?

The p:t AKT ratio does not change consistently across all gRNAs (Figure 5C) but we can look at Akt (total) protein levels and include this information if needed.

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7) Stats should be added directly on the graphs for the recycling assays, doing a pairwise comparison of the different genotypes for each time points. Can the authors clarify what the t-32min quantification graphs adds (fig7E, supp fig S8G-I)? I would advise to remove them, as this data is already presented in the recycling assay graphs. __

We don't include these because although they are technical replicates, they are demonstrative of a single experiment. What we include instead is the quantitation across independent biological experiments (which each have their own internal multiple technical replicates), where it is appropriate to include statistical analysis.

8) There is a substantial amount of typos and erroneous references to figures. I listed below the ones that I spotted and I encourage the authors to carefully check.

1. there are some mistakes in referencing the number of cysts in supp table 1. There is for example no cysts experiments in Figure 1 but yet there are some references to figure 1 in supp table 1. Please correct it. I think it will be easier for the reader if the number of cysts quantified for each conditions was also indicated in the figure legends. Supp table 1 can still be included for readers that want additional details.
2. comma missing page 3
3. page 3 and 4: PI(3,4)2 means PI(3,4)P2? Can be shorten to PIP2 for ease of read and specify if it is another PIP2 specie otherwise
4. define CYTH abbreviation: I suppose this is for cytohesin?
5. fig1F-I: don't understand why TCGA.OV is specified on some but not all the graphs. It seems to me that all the data are from TCGA.OV? Makes it seems it is nit the case
6. legend of fig1H, I: y axis is -Log10 values in 1I, not Log10 values
7. page 6: dKO abbreviation is already specified above and should be used to avoid repetition and for ease of read
8. supp fig S1D: missing legend for the second bar (after Wild Type)
9. supp fig S1N: legend of the X-axis should be below the axis
10. supp fig S1O: the numerotation of the X-axis needs to be below the line of the axis for ease of read, not above it
11. legend of S2A: clones 1.12 and 1.15 are p53-/-;PTEN-/- and not PTEN-/-
12. supp figS2C can the authors specify the different stages of matrigel (liquid or gel) that are used for the invasion assay, to make it easier for the non-specialist to understand what is going on. Please confirm that the 50% GFR matrigel makes a gel on top of the cells and fill in the wound to produce the 3D invasion assay setup.
13. page 7: no parental cells are used in S3A, B only p53 null and p53 null and dKO. Please also specify what cells are being compared in the text
14. description of arrow heads and colours need to be moved to figure legends and not in main text (page 7)
15. fig 2D: the signification of the dot in the circles needs to be in the legends (since it is its first apparition in the manuscript). It only appears later on, in supp2A legend. Additional description of the matrices is necessary, as they contain a lot of information to digest to understand fully what is going on
16. legend of fig3: error in figure reference: area data is D and not E, protrusive phenotypes are E and not F
17. arrow missing in fig3B
18. fig 3D,E, G, H: please indicate the cell line studied
19. fig 3I: the different genotypes need to be stated on the galleries for clarity
20. page 8: define Arf6-mNG in the text
21. __ page 9: "We thank the reviewer for their careful examination of the manuscript. We will go through all above points and make the corresponding careful adjustments to the manuscript.

OPTIONAL SUGGESTIONS

1) Choice of cell line: There is a high number of patients (around 9% according to (Cole et al. 2016)) that present the R248Q gain-of-function mutation. A recent study has shown that this mutant p53 protein is associated to an activation of Akt signalling and an increase of the intercellular trafficking of EGFR (Lai et al. 2021). Given that EGFR was also a hit in this screen, that is seems to have a central role in Arf6 cargoes (fig 4G), I think it would be a great addition to this study. It could hence cooperate with PTEN loss to drive strong, robust invasion.

This is an excellent observation and one we will likely follow-up in an independent study.

2) Are MAPK involved in the PTEN KO pro-invasive phenotype? In particular Erk1/2, since EGFR is one of the PTEN loss induced Arf6 cargoes.

This is an excellent observation and one we will likely follow-up in an independent study.

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REFERENCE Cole, Alexander J., Trisha Dwight, Anthony J. Gill, Kristie-Ann Dickson, Ying Zhu, Adele Clarkson, Gregory B. Gard, et al. 2016. « Assessing Mutant P53 in Primary High-Grade Serous Ovarian Cancer Using Immunohistochemistry and Massively Parallel Sequencing ». Scientific Reports 6 (1): 26191. _https://doi.org/10.1038/srep26191_.

Lai, Zih-Yin, Kai-Yun Tsai, Shing-Jyh Chang, et Yung-Jen Chuang. 2021. « Gain-of-Function Mutant TP53 R248Q Overexpressed in Epithelial Ovarian Carcinoma Alters AKT-Dependent Regulation of Intercellular Trafficking in Responses to EGFR/MDM2 Inhibitor ». International Journal of Molecular Sciences 22 (16): 8784. _https://doi.org/10.3390/ijms22168784_. __

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

The authors have conducted a study of the molecular requirements for cancer invasion that is stunning in its thoroughness and depth and breadth of its molecular analysis. The writing is exceptionally precise though also very dense (see below). The molecular model proposed is that PTEN loss (in a p53 null background) leads to reliance upon ARF6 for invasion, with regulation through interactions with AGAP1 and beta1-integrin and it is convincingly demonstrated. They focus on interpreting the consequences of genetic and pharmacologic manipulations in a cell line, using a series of 2D and 3D assays. The phenotypes are more prominent in 3D assays.

Concerns and Suggestions:

• There is a disconnect between the essentially complete loss of protrusions and invasion in 3D (e.g. 4A) and the reduction in magnitude of protrusive invasion but the continued presence of elongated cells with protrusions in 2D (e.g. S4C). This discrepancy is present in a couple of comparisons and is glossed over in quick callouts to many figure panels.

  We thank the reviewer for mentioning this as this comment was very helpful in determining that we needed to clarify our description of the role of ARF6 to protrusion formation vs maturation. In the Trp53-/- genotype, protrusions can form, but they rapidly retract, failing to mature into structures that drive invasion through ECM (e.g. Figure S2E). This protrusion maturation occurs upon PTEN KO. When ARF6 depleted, PTEN-null cells can form protrusions, but now again lack the ability to mature into invasion-inducing structures.

This concept of needing ARF6 for protrusion maturation and maintenance is underpinned by our model of ARF6 regulating recycling of active integrin back to the protrusion front. Indeed, we have observed ARF6 being required not for protrusion initiation, but rather ensuring protrusions are not retracted in other contexts (i.e. upon loss of the ARF6 GEF protein IQSEC1 in invading 3D culture of PC3 cells; PMID: 33712589).

We also note that, as responded to Reviewer 1, the assay is a 3D invasion rather than 2D migration assay, with cells sandwiched between Matrigel.

We will update the relevant sections of the results and discussion with the point above.

Once a journal has been identified, it would be wise for the editor to allow some flexibility in word limit to enable some very dense sections to be expanded slightly to guide the reader through the experiments and results more clearly. For example, in the section "ARF6 regulates active integrin pools...", there are callouts like (Fig. 7C,E; S8A-C; G-I) and then (Fig. 7D,E; Fig. S8E-F, H-I). It takes a lot of time to unpack these different experimental claims based on a single sentence.

We greatly appreciate the refreshing comments of this reviewer to advocate for actions to improve clarity in our reporting. We would take glad advantage of such a possibility.

The patient data on CYTH2 and its relationship to survival is modestly convincing.

In Ovarian Cancer, effects on survival are often minor. This is not a disease where one often sees large shifts in survival, which is why we are so excited about the large shifts that we do see with the ARF GTPase module we identified. However, we concede that the effects on CYTH2, although significant, are not vast changes. We will point this out and tone down our language.

Very minor- search on %- there are a few inconsistencies in terms of spaces and commas vs. periods. The Methods also have some inconsistencies in terms of spaces between numbers and units or numbers and degrees Celsius. References are also in a different font. Overall it was extremely carefully written though (just dense).

We thank the reviewer for their careful inspection of our manuscript. We will carefully go over the sections flagged before resubmission

Reviewer #2 (Significance (Required)):

One limitation of the experimental design is that the depth of molecular analysis in vitro comes at the expense of any in vivo validation, which the authors acknowledge in the Discussion. They attempt to make similar points using analysis of patient survival data from public databases but these analyses generally yielded small magnitude differences. The main audience for this study is likely to be cell biologists interested in cell migration, cell-ECM adhesion, cancer invasion, and GTPases. I don't see any need for new experiments- what can be done has been done and then some. I do think that it would benefit readers if the text could be made less dense.

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

Summary: Using a murine HGSOC 3D cell model, in combination with analysis of human ovarian cancer datasets, the authors uncover a CYTH2-ARF6-AGAP1 signaling module regulated by PTEN and identify a biomarker for tumor invasion and targeted therapy.

Major comments:

__The findings of this study are significant as they reveal a critical signaling module that controls tumor invasion by mediating tumor cell interaction with the extracellular matrix. The experiments are properly designed, and the data are well presented. The conclusions are appropriate and supported by the data. The limitation of the study has also been discussed properly.

One suggestion regarding the survival analysis in Fig. 6 and 7. __

The authors noted that the CYTH2-ARF6-AGAP1 module is not specifically or only induced in Pten-null contexts, but rather that Pten-null cells become more dependent on the module for enacting the invasive phenotype. Based on this, it would be interesting to evaluate how the PTEN status impacts the survival difference by integrating the PTEN genomic status (WT versus mutation) or its expression level (protein or mRNA) into the survival analysis of patient cohorts in Fig. 6 and Fig. 7.

We thank the reviewer for this excellent point. We will include such analysis, where possible. One consideration will be that extensive division of patients based on these molecular characteristics may results in patient numbers too low to draw conclusions of significance.

**Referees cross-commenting**

Gene deletion and mutation may elicit different functional outcomes. I therefore agree with Reviewer #1 that "the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained".

We will make our reasons for this choice clear in the text before submission. Please refer to response to Reviewer 1, Major comment 1.

Reviewer #3 (Significance (Required)):

The model used and data presented in this study are of significance for both scientific discovery and clinical application, which will interest the broad audience in both basic and clinical research.

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

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

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:

Using a murine HGSOC 3D cell model, in combination with analysis of human ovarian cancer datasets, the authors uncover a CYTH2-ARF6-AGAP1 signaling module regulated by PTEN and identify a biomarker for tumor invasion and targeted therapy.

Major comments:

The findings of this study are significant as they reveal a critical signaling module that controls tumor invasion by mediating tumor cell interaction with the extracellular matrix. The experiments are properly designed, and the data are well presented. The conclusions are appropriate and supported by the data. The limitation of the study has also been discussed properly.

One suggestion regarding the survival analysis in Fig. 6 and 7. The authors noted that the CYTH2-ARF6-AGAP1 module is not specifically or only induced in Pten-null contexts, but rather that Pten-null cells become more dependent on the module for enacting the invasive phenotype. Based on this, it would be interesting to evaluate how the PTEN status impacts the survival difference by integrating the PTEN genomic status (WT versus mutation) or its expression level (protein or mRNA) into the survival analysis of patient cohorts in Fig. 6 and Fig. 7.

Referees cross-commenting

Gene deletion and mutation may elicit different functional outcomes. I therefore agree with Reviewer #1 that "the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained".

Significance

The model used and data presented in this study are of significance for both scientific discovery and clinical application, which will interest the broad audience in both basic and clinical research.

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 #2

Evidence, reproducibility and clarity

The authors have conducted a study of the molecular requirements for cancer invasion that is stunning in its thoroughness and depth and breadth of its molecular analysis. The writing is exceptionally precise though also very dense (see below). The molecular model proposed is that PTEN loss (in a p53 null background) leads to reliance upon ARF6 for invasion, with regulation through interactions with AGAP1 and beta1-integrin and it is convincingly demonstrated. They focus on interpreting the consequences of genetic and pharmacologic manipulations in a cell line, using a series of 2D and 3D assays. The phenotypes are more prominent in 3D assays.

Concerns and Suggestions:

1. There is a disconnect between the essentially complete loss of protrusions and invasion in 3D (e.g. 4A) and the reduction in magnitude of protrusive invasion but the continued presence of elongated cells with protrusions in 2D (e.g. S4C). This discrepancy is present in a couple of comparisons and is glossed over in quick callouts to many figure panels.
2. Once a journal has been identified, it would be wise for the editor to allow some flexibility in word limit to enable some very dense sections to be expanded slightly to guide the reader through the experiments and results more clearly. For example, in the section "ARF6 regulates active integrin pools...", there are callouts like (Fig. 7C,E; S8A-C; G-I) and then (Fig. 7D,E; Fig. S8E-F, H-I). It takes a lot of time to unpack these different experimental claims based on a single sentence.
3. The patient data on CYTH2 and its relationship to survival is modestly convincing.
4. Very minor- search on %- there are a few inconsistencies in terms of spaces and commas vs. periods. The Methods also have some inconsistencies in terms of spaces between numbers and units or numbers and degrees Celsius. References are also in a different font. Overall it was extremely carefully written though (just dense).

Significance

One limitation of the experimental design is that the depth of molecular analysis in vitro comes at the expense of any in vivo validation, which the authors acknowledge in the Discussion. They attempt to make similar points using analysis of patient survival data from public databases but these analyses generally yielded small magnitude differences. The main audience for this study is likely to be cell biologists interested in cell migration, cell-ECM adhesion, cancer invasion, and GTPases. I don't see any need for new experiments- what can be done has been done and then some. I do think that it would benefit readers if the text could be made less dense.

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Referee #1

Evidence, reproducibility and clarity

This paper by Konstantinou et al aims at deciphering the mechanisms by which PTEN loss could be driving poorer prognosis in patients. The authors use their great high-throughput 3D screening method coupled to an unbiased proteomic method and a CRISPR screen to uncover a new pro-invasive axis driving collective invasion of high-grade serous ovarian carcinoma (HGSOC) cells. Overall, this is a very impressive study, very well done and controlled with rigorous statistical analyses that uses sophisticated methods to convincingly show that the CYTH2-ARF6-AGAP1-ITGA6/ITGB1 module is required for the pro-invasive effect of PTEN depletion and discriminates patients with poorest prognosis.

Major comments

Below are listed all the claims that, in my opinion, are not adequately supported by the data.

1. Choice of the cell line: More justification on the use of the ID8 cell line and on the p53 deletion is needed. The authors need to clearly state that most p53 mutations in ovarian cancer are missense mutations that lead to a strong accumulation of a p53 protein devoid of transcriptional activity. Nevertheless, it seems that p53 mutations are not associated to differences in patient survival. Hence the choice of studying PTEN loss in the complete absence of p53, a situation that does not mirror the clinical situation, needs to be explained. Moreover, the in vivo experiments already performed in the literature mentioned in the discussion should be mentioned in the introduction to provide more context and physiological relevance to this study (especially regarding the special focus on the p53 null/ dKO cells throughout the study).
2. "Therefore, PTEN loss in ovarian cancer, particularly at the protein level, occurs in the tumour epithelium and is associated with upregulated AKT signalling and poor overall survival". This claim is an over-interpretation and over-generalisation of the data presented. I appreciate the honesty of the authors in showing all the ovarian datasets that are available and highlight the discrepancies in expression of the proteins they study in stroma and epithelium. I think the way to present these data in the text without over-interpreting and generalizing would be to show that there is a clear epithelial-specific downregulation of PTEN at the mRNA level. Most likely due to the contribution to other cell types in the stroma, only 3 out of 5 bulk tumour mRNA datasets show a tumour specific downregulation of PTEN and no association with survival based on a median split of PTEN mRNA expression. Nevertheless, although there is no direct correlation between PTEN mRNA and protein levels, patients with low PTEN protein levels have poorer survival that is associated to an upregulation of Akt signalling. This allows to have a clearer conclusion, based solely on the protein data presented and no over-generalisation using the mRNA data. This, to me, makes a stronger case for studying PTEN loss in ovarian cancer and is fully supported by the data presented.
3. PTEN loss induces modest effects in 2D culture. The authors make claims regarding the fact that some of the phenotypes they look at happen after PTEN depletion alone or in combination with p53 loss and are more prominent in 3D vs 2D. Many of these are insufficiently backed up by data. A few key experiments are also only performed in 2D and should be done in 3D. Finally, some clarifications if the role of PTEN is most prominent on either collective, ECM-induced or 3D-dependent invasion.

First, the authors claim that PTEN loss alone (i.e. without p53 deletion) leads to changes in Akt signalling. Supp fig 1H clearly shows that there is no significant increase in Akt activation, although there seems to be one in the Western Blot (WB) presented in supp fig 1G. There is a clear, significant increase in the Akt activation in all the PTEN KO clones when in association with p53 loss though. This claim is hence not backed up by data and the conclusion seems to be that the effect on Akt signalling requires both deletion of p53 and PTEN.

It will be interesting to see a quantification of the pS473-Akt staining (supp fig S1J), as it seems from these images that pAkt is preferentially found on rounded cells. It should also be performed in 3D conditions to see if there is an enrichment at invasive tips and back-up the invasion data.

Arf6 is recruited to the invasive tips of cells invading a 2D wound (fig4D). How do the authors reconcile the fact that all the machinery required for 3D invasion is present but that PTEN loss has a modest effect on cells in 2D? If the wound assay was done on glass, it should be done again on ECM coated glass to see if it recapitulates the effects seen in 3D. This experiment will help deconvolute if the effect of PTEN loss is more linked to collective behaviour than 3D organization or presence of ECM.

The recycling assays are all done in 2D, condition under which the authors claim that the PTEN phenotype is weakest. Although I understand that it is not possible to do this assay in 3D, its contribution to elucidating the mechanism by which integrins participate in the PTEN loss invasive phenotype is not clear. The requirement of integrins relies on the data showing that ITGB1 KO results in no collagen4-positive basement membrane of the cysts and greatly impaired invasion. Experiments looking at the integrin localisation would be helpful: can an enrichment at the invasive tips can be seen? Are ITGA6 and/or ITGB1 repartitions homogeneous between the cysts membranes and the invasive tips? In my opinion the Src/FAK data is not enough to draw the conclusions of fig7I schematic. 4. Expression of AGAP1 isoforms do not alter ARF6 levels. Data in fig 6C, D show a significant downregulation of Arf6 and Akt signalling after expression of AGAP1S. Can the authors clarify what they mean? 5. Arf6 is not modulated in the different cell lines: data in fig4B (far right graph) and supp fig 4B, J seem to indicate otherwise. Can the authors clarify what they mean? 6. Immunofluorescence panels without quantifications: Quantifications for the different stainings shown in fig3A; 4D, E; 5H; 7B and supp fig S1L, J; S3 need to be included to fully back the conclusions of the authors. Indeed, these images are used to draw conclusions and not only as illustrations. 7. Quantifications of invasion show that WT cysts become hyper-protrusive at around the half experiment mark (around 30-40hrs). Nevertheless, all movies or galleries show spherical cysts, which does not seem representative. Can the authors change this or explain why these images/movies were chosen? 8. Since it seems that the main effect of PTEN is to drive the localisation and intensity of recycling of Arf6 cargoes, it will be helpful to confirm that all the proteins involved in the Arf6 module be shown to be accumulated/present at the pro-invasive tips. Immunofluorescence stainings showing the presence of AGAP1 (could be done with the AGAP1S isoform that is mNeon-tagged), pS473-Akt, ITGB1 (active integrin if possible, otherwise total integrin), ITGA5, PI3K should be included if possible. A quantification comparing signal in the cysts and in the invasive tips should also be included to see if there is an accumulation to PIP3-enriched areas. 9. Data in fig5I convincingly show that PTEN loss induces a fragmented collagen4-positive basement membrane. The authors use this data to claim that this is one of the ways that PTEN could be driving invasion but no correlation between these structures and the hyper-protrusive phenotype is made. This experiment needs to be done to support this claim.

Minor comments

1. Data visualization: I think that the heatmap representation is overkill when only 2 or 3 conditions are presented. A graph showing the evolution of area or spherical/Hyper-protrusive phenotype proportions across time would be easier to read and more impactful: each genotype could be presented with a colour and the spherical/hyper-protrusive phenotypes as either plain or dashed lanes across time. I understand that this representation allows for the stats to be done at each time points but they are generally pretty clear (especially for the PTEN KO or dKO phenotypes) and do not need to be done for each time point in my opinion. These heatmaps could be put in supplementary figures if the authors feel strongly about putting stats for each time points.

Fig supp S1M, fig 5I should be presented as a stacked histogram to improve readability and merged with fig supp S1K.

Displaying fold change as antilog rather than log values would be easier for the reader to realise the magnitude of the differences.

A bar graph would be easier to read than the matrix representation for fig 6B.

The way Area data is presented throughout to me makes it very difficult to understand what is going on. Could the authors at least give some explanations in figure legends. A curve graph displaying the evolution of the area across time would be easier to read and see the differences between conditions. 2. It is confusing that, in fig supp S1M, there is a significant decrease of the rounded phenotype after PTEN loss that is not associated to a significant change in another of the categories. Could the authors explain how? 3. One of the big differences of the PTEN KO cells seems their ability to invade through the matrigel bed and migration on the glass below (supp movie S2). From what I gather, these cysts would be considered out of focus and excluded from the analysis. Would it be possible that this would minimize some of the results? Would it be possible to include a quantification of this particular phenotype to confirm it is specific to PTEN KO cells?

In the same spirit, could the authors provide the percentage of non-classified cysts, to make sure that the same proportion of cysts is quantified across all different genotypes. 4. Can the authors clarify how a 0 fold change (in log value) in fig 2D can be highly significant? 5. Delta isoform of PI3K seems to have an effect on area in the middle of the experiment, but has no effect at all on invasion. Could the authors comment? Are these smaller cysts still as invasive? There might be an interesting uncoupling between proliferation and invasion there. 6. ITGB1 depletion seems to induce a downregulation of Akt protein. Is that right? Does it change Akt localisation? Is there a dose effect whereby there is not enough Akt protein to mediate invasion? 7. Stats should be added directly on the graphs for the recycling assays, doing a pairwise comparison of the different genotypes for each time points. Can the authors clarify what the t-32min quantification graphs adds (fig7E, supp fig S8G-I)? I would advise to remove them, as this data is already presented in the recycling assay graphs. 8. There is a substantial amount of typos and erroneous references to figures. I listed below the ones that I spotted and I encourage the authors to carefully check.

• a. there are some mistakes in referencing the number of cysts in supp table 1. There is for example no cysts experiments in Figure 1 but yet there are some references to figure 1 in supp table 1. Please correct it. I think it will be easier for the reader if the number of cysts quantified for each conditions was also indicated in the figure legends. Supp table 1 can still be included for readers that want additional details.
• b. comma missing page 3
• c. page 3 and 4: PI(3,4)2 means PI(3,4)P2? Can be shorten to PIP2 for ease of read and specify if it is another PIP2 specie otherwise
• d. define CYTH abbreviation: I suppose this is for cytohesin?
• e. fig1F-I: don't understand why TCGA.OV is specified on some but not all the graphs. It seems to me that all the data are from TCGA.OV? Makes it seems it is nit the case
• f. legend of fig1H, I: y axis is -Log10 values in 1I, not Log10 values
• g. page 6: dKO abbreviation is already specified above and should be used to avoid repetition and for ease of read
• h. supp fig S1D: missing legend for the second bar (after Wild Type)
• i. supp fig S1N: legend of the X-axis should be below the axis
• j. supp fig S1O: the numerotation of the X-axis needs to be below the line of the axis for ease of read, not above it
• k. legend of S2A: clones 1.12 and 1.15 are p53-/-;PTEN-/- and not PTEN-/-
• l. supp figS2C can the authors specify the different stages of matrigel (liquid or gel) that are used for the invasion assay, to make it easier for the non-specialist to understand what is going on. Please confirm that the 50% GFR matrigel makes a gel on top of the cells and fill in the wound to produce the 3D invasion assay setup.
• m. page 7: no parental cells are used in S3A, B only p53 null and p53 null and dKO. Please also specify what cells are being compared in the text
• n. description of arrow heads and colours need to be moved to figure legends and not in main text (page 7)
• o. fig 2D: the signification of the dot in the circles needs to be in the legends (since it is its first apparition in the manuscript). It only appears later on, in supp2A legend. Additional description of the matrices is necessary, as they contain a lot of information to digest to understand fully what is going on
• p. legend of fig3: error in figure reference: area data is D and not E, protrusive phenotypes are E and not F
• q. arrow missing in fig3B
• r. fig 3D,E, G, H: please indicate the cell line studied
• s. fig 3I: the different genotypes need to be stated on the galleries for clarity
• t. page 8: define Arf6-mNG in the text
• u. page 9: "<" symbol should be an alpha symbol
• v. fig 4A: indicate the cell line used on the figure
• w. supp fig S4E: why is it specified mouse-specific for the shArf6?
• x. 4H, I, J: indicate on the figure if these interactors are mostly unchanged, strong interactors or weak interactors for clarity
• y. legend of fig4H: "coloured spots underneath denote the protein complex that each interactor belongs (in J)" should indicate panel G and not J
• z. fig4I, J: are you sure of the legend for the fold change coloring? Log2 of 1 is a 0 fold change, i don't see how these could show any significant difference (i.e. some of the pale red circles are significant)
• aa. page 11: description of the assay (starting with "Machine learning classification of...") is very confusing, please clarify
• bb. page16: figure 4H should be 4I (PTEN-null specific association of Arf6 with ITGA5)
• cc. supp fig S5H-P: choose Tumour or cancer to homogeneise naming across the graphs
• dd. fig 5H: box are difficultly visible in green, change color to yellow or something more visible
• ee. page 13: Fig6E, F should also refer to 6G
• ff. LCM abbreviation on page 10 and 12 refers to LCMD? Otherwise please define it.

Optional suggestions

1. Choice of cell line: There is a high number of patients (around 9% according to (Cole et al. 2016)) that present the R248Q gain-of-function mutation. A recent study has shown that this mutant p53 protein is associated to an activation of Akt signalling and an increase of the intercellular trafficking of EGFR (Lai et al. 2021). Given that EGFR was also a hit in this screen, that is seems to have a central role in Arf6 cargoes (fig 4G), I think it would be a great addition to this study. It could hence cooperate with PTEN loss to drive strong, robust invasion.
2. Are MAPK involved in the PTEN KO pro-invasive phenotype? In particular Erk1/2, since EGFR is one of the PTEN loss induced Arf6 cargoes.

Reference

Cole, Alexander J., Trisha Dwight, Anthony J. Gill, Kristie-Ann Dickson, Ying Zhu, Adele Clarkson, Gregory B. Gard, et al. 2016. « Assessing Mutant P53 in Primary High-Grade Serous Ovarian Cancer Using Immunohistochemistry and Massively Parallel Sequencing ». Scientific Reports 6 (1): 26191. https://doi.org/10.1038/srep26191.

Lai, Zih-Yin, Kai-Yun Tsai, Shing-Jyh Chang, et Yung-Jen Chuang. 2021. « Gain-of-Function Mutant TP53 R248Q Overexpressed in Epithelial Ovarian Carcinoma Alters AKT-Dependent Regulation of Intercellular Trafficking in Responses to EGFR/MDM2 Inhibitor ». International Journal of Molecular Sciences 22 (16): 8784. https://doi.org/10.3390/ijms22168784.

Significance

It has only been recently appreciated that PTEN loss is a driver in ovarian cancer (Martins et al. 2020) but no studies to data have aimed at understanding the mechanisms. This study is hence the first to propose one and as such provides a very valuable advance for researchers interested in ovarian cancer. The authors also propose that the CYTH2-ARF6-AGAP1 high mRNA be used as a signature of worsen prognosis. This hence paves the way to better understanding and stratify patients with ovarian cancers.

One of the main difference after PTEN loss is the accumulation of PIP3 in pro-invasive tips that correlates with the recruitment of Arf6 to these tips. The authors have developed a very powerful automated quantification pipeline to follow the behaviour of cysts grown in 3D that they have coupled to an unbiased proteomic method to identify interactors and a CRISPR screen to test their functional relevance. This is clearly the strongest aspect of the paper that allows them to gather very robust data and identify the machinery driving invasion in PTEN KO cells. The authors' model claims that this in turns recruit the Arf6 machinery, composed of CYTH2 2G (the only CYTH2 isoform correlated to a poorer prognosis, preferentially binding PIP3) and AGAP1 that leads to a local increase in active integrin recycling that mediates the more invasive phenotype of PTEN depleted cells. It is rightfully mentioned in the discussion that PTEN depletion only leads to a modest change in Arf6 interactors, and that most likely PTEN loss acts by locally directing the Arf6 machinery to the invasive tips. Indeed, the authors convincingly show that Arf6, AGAP1 and ITGB1 are required for the formation of these invasive protrusions.

The limitation of this study is the combination of 2D and 3D experiments to drive general conclusions on the mechanism. These are listed in the previous section. Another big limitation, in my opinion, is the choice of the cell model: indeed, nearly all patients present a vast increase in the amount of the p53 protein present due to a very large number of mutations that in most cases prevent its binding to DNA. Throughout this paper the authors have used a p53 null cell line that expresses no p53 protein. This is not compatible with the clinical situation. Moreover, since p53 also present frequent gain-of-function mutations that have been shown to be associated to an increase of Akt signalling and intercellular trafficking of EGFR. Studying the implication of the Arf6 module identified here in a context of p53 WT or mutant protein overexpression would be of great interest.

Reference

Martins, Filipe Correia, Dominique-Laurent Couturier, Anna Paterson, Anthony N. Karnezis, Christine Chow, Tayyebeh M. Nazeran, Adekunle Odunsi, et al. 2020. « Clinical and Pathological Associations of PTEN Expression in Ovarian Cancer: A Multicentre Study from the Ovarian Tumour Tissue Analysis Consortium ». British Journal of Cancer 123 (5): 793‑802. https://doi.org/10.1038/s41416-020-0900-0.

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Reply to the reviewers

1. General Statements [optional]

We are grateful to the reviewers for highlighting the value and power of our 3D chimeric dataset to explore cancer/stellate interactions in pancreatic cancer invasion. We also appreciate their support of our findings identifying divergent roles for the two related enzymes ADAMTS2 and ADAMTS14. We thank the reviewers for their detailed comments, which have allowed us to prepare a significantly stronger and clearer manuscript.

Following the reviewers comments we have made three major changes to the manuscript, which we will outline here in addition to the point-by-point rebuttal.

1. i) Revised manuscript structure. We have modified the structure of the manuscript, which we hope improves the clarity and accessibility of the work.

Figure 1 remains the description of our 3D invasion model and our approach to identify stellate cell and cancer cell transcriptomic information from this context.

Figure 2 describes our focus on proteases and now includes concordance of our data with clinical data sets. This is also now where we describe the strikingly opposing roles for ADAMTS2 and ADAMTS14 in regulating invasion.

Figure 3 is now the figure demonstrating that ADAMTS2 and ADAMTS14 have an equal contribution to collagen processing from stellate cells. This is an important experiment given that the main physiological roles for these enzymes are in the processing of collagen, and the importance of collagen for cancer progression. It was therefore reasonable to hypothesise that the effect of these enzymes on invasion could be due to differences in their collagen processing in this context. The finding that both have an equal effect on collagen processing points towards a wider, and more diverse, role for these enzymes in regulating biology.

Figure 4 describes the divergent roles of these two enzymes on myofibroblast differentiation, and by extension TGFβ bioavailability. In this figure we now include experiments with TGFβ reporter constructs, which demonstrate an increase in active TGFβ following loss of ADAMTS14 and a reduction in TGFβ activity following loss of ADAMTS2.

Figure 5 is our matrisomic experiment to identify enriched enzyme-specific substrates following knockdown of either ADAMTS2 or ADAMTS14.

Figure 6 details our investigation into the substrate responsible for the reduction in invasion following loss of ADAMTS2. As the previous matrisomic experiment identified only two enriched ADAMTS2 substrates, we investigated both in our 3D assays, identifying SERPINE2 as the responsible substrate. Further analysis identified a reduction in plasmin activity in ADAMTS2 deficient cells. This was rescued with co-knockdown of SERPINE2, implicating this pathway as being crucial for mediating the effect of ADAMTS2. Additionally, we now include experiments demonstrating that concomitant knockdown of SERPINE2 alongside ADAMTS2 rescues the reduction in TGFβ activity observed with ADAMTS2 loss alone.

Figure 7 describes our analysis of ADAMTS14 substrates. As the matrisomics identified a large change in proteins following ADAMTS14 knockdown, we performed an siRNA screen of candidates to identify those responsible for ADAMTS14 phenotype. This, followed by further validation in our 3D invasive assay, revealed Fibulin2 as the responsible substrate. Fibulin2 has a well-established role in regulating TGFβ release from the matrix. In accordance with this we present new data using TGFβ reporter constructs, which demonstrate that the increase in active TGFβ following ADAMTS14 knockdown can be reversed with co-knockdown of Fibulin2.

1. ii) Improvement of the clinical significance of our chimeric data set and ADAMTS proteins. Ideally, we would like to present IHC images of ADAMTS2 and ADAMTS14 expression in PDAC tissue samples to corroborate our in vitro findings. However as these enzymes are secreted, this precludes antibody based imaging, as it would not provide cell type specific information. RNA scope presents an alternative, however we have experienced technical issues with this technique due to RNA degradation in PDAC tissue and unavailability of ADAMTS2/14 specific probes. In place of this we have used a range of publically available resources.

We have compared our chimeric data set with human clinical data using the resource published by Maurer and colleagues (PMID: 30658994). This paper presents transcriptomic data from PDAC tumour and stromal compartments using laser microdissection of clinical tissue. In accordance with our data set, the majority of metzincins, including ADAMTS2 and ADAMTS14, are expressed in the stromal compartment. These data are presented in updated figure 2.

We have also examined ADAMTS2 and ADAMTS14 expression in PDAC and CAF subtypes using publically available data sets. Using the TCGA dataset, we identified that ADAMTS2 and ADAMTS14 are highly expressed in PDAC tumours compared to normal counterparts. As the majority of PDAC is comprised of stroma, the bulk transcriptomic data from TCGA, combined with the results from the Maurer publication, lead us to conclude that this expression reflects the stromal origin of these proteases. In addition, using publically available single cell RNA sequencing data published by Luo and colleagues (PMID: 36333338), we identified ADAMTS2 and ADAMTS14 expression in the prominent PDAC CAF subtypes, inflammatory and myofibroblastic CAFs. Together these data demonstrate that these enzymes are enriched in clinical disease, which when combined with our mechanistic 3D studies implies a greater role for these enzymes in disease progression than previously appreciated.

iii) Improved mechanistic link between ADAMTS2 and ADAMTS14 with TGFβ bioavailability

To strengthen the association between ADAMTS2 and ADAMTS14 function, their substrates SERPINE2 and Fibulin2, and TGFβ bioavailability, we have performed the following experiments using TGFβ reporter constructs:

We have taken conditioned media from stellate cells lacking either ADAMTS2 or ADAMTS14, along with co-knockdown of their substrate, and stimulated a recipient cell line expressing a SMAD Luciferase reporter. These cells express luciferase in response to TGFβ stimulation. In accordance with a role for ADAMTS14 and Fibulin2 in regulating TGFβ, we demonstrate that following ADAMTS14 knockdown there is a strong increase in active TGFβ in the media (Figure 4I), which is abrogated with co-knockdown of Fibulin2 (Figure 7F).

We have also obtained a fluorescent reporter, CAGA-eGFP, which expresses GFP in response to TGFβ stimulation in order to examine TGFβ activity in 3D cultures. Stellate cells expressing this construct were embedded in collagen: Matrigel hydrogels following knockdown of either ADAMTS2 or ADAMTS14 and CAGA fluorescence recorded after 72 hours of culture. In accordance with our data, stellate cells deficient in ADAMTS14 showed increased fluorescence in 3D, indicative of increased TGFβ activity, which was abrogated with co-knockdown of Fibulin2 (Figure 4J, K and 7G, H). Equally, loss of ADAMTS2 reduced TGFβ activity in 3D culture, which was rescued with co-knockdown of SERPINE2 (Figure 4J, K and 6 D, E).

These experiments confirm a link between the ADAMTS enzyme, its relevant substrate, and TGFβ bioavailability. Together with extensive published work linking SERPINE2 and Fibulin2 with TGFβ release we are confident in our proposed mechanism for the dichotomic relationship of ADAMTS2 and ADAMTS14 in regulating TGFβ and thus myofibroblast action.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

• *

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

• *

This study aims to explain the opposing contributions of stromal stellate cells/CAFs to PDAC. By first identifying stroma-specific proteases, followed by a process of candidate selection and elimination, the authors find that two specific metalloproteases that share enzymatic activity against collagen in fact have differential activity on TGFb availability. This could be interpreted as a way of shaping the CAF population and tumor-promotin or -restricting properties of the stroma.

There are several flaws that the authors could address to improve the manuscript:

1. In the flow of experiments and analyses, there is a strange mix of fully unbiased discovery phases followed by functional experiments that do not consider all possible candidates to test, and vice versa. For instance, from the mixed-species transcript analysis, ADAMTS2 and -14 are chosen based on their shared collagenase activity based on literature. However, the authors then perform again a proteomics analysis to identify things from the entire matrisome that are cleaved by these enzymes? Then, for ADAMTS2 a co-silencing approach is done on one selected candidate (Serpine2), but for ADAMTS14 an siRNA screen is performed? The problem of this approach is that the rationale for some studied enzymes is very strong, where as for others it is not.

We thank the reviewer for their comment and trust the revised manuscript provides more clarity for the rationale of our approach. We performed the chimera sequencing as a discovery experiment to reveal the communication between cancer and stellate cells in a 3D, invasive context. We present the chimera experiment and data here as a resource for the community, with our analysis of ADAMTS2 and ADAMTS14 function serving as a first example of the biological insight this data set can reveal. Other insights revealed from this dataset are active avenues of research in our group.

Our finding that ADAMTS2 and ADAMTS14 have dramatically opposing roles in regulating invasion was especially striking given their equal contribution to collagen processing in this context. This led us to conclude that the divergent nature of these enzymes must be due to enzyme-specific substrates. A substrate repertoire for these enzymes has been previously published (PMID: 26740262) and we reasoned that the responsible substrate would be enriched following knockdown of the relevant enzyme. Thus we preformed matrisomics on cells lacking either of these enzymes, which did indeed reveal enrichment of known, enzyme-specific substrates that we could use for further analysis.

The matrisome following ADAMTS2 knockdown was minimally changed and only presented enrichment of two ADAMTS2 substrates. As there was only a minimal cellular phenotype in 2D following loss of ADAMTS2, we decided to concentrate our studies on the two identified substrates in our 3D assay. Conversely as the matrisome following ADAMTS14 knockdown was dramatically different from control cells, and ADAMTS14 knockdown presented a clear phenotype in αSMA expression, we decided to perform a screen of all matrisome hits. This highlighted the role of IL-1β in mediating myofibroblast differentiation, which has been reported elsewhere and validated our approach. Further, this refined the number of enriched ADAMTS14 substrates to two, MMP1 and Fibulin2, with Fibulin2 being identified as the responsible candidate in our 3D assays.

The ECM is more than just collagen. Choosing these two metalloproteases based on their shared collagen substrate is an approach that perhaps oversimplifies the ECM a bit, and again, does not provide the strongest rationale that these metalloproteases are most likely to explain counteracting stromal activities on tumor growth and progression.

We fully agree with the reviewers comment and feel our work acutely demonstrates this point. Loss of either ADAMTS2 or ADAMTS14 had similar effects on collagen processing; implicating their divergent roles on invasion was independent of their effects on collagen regulation. This work therefore showcases the incredible complexity of ECM regulation in tumour progression. As discussed in the manuscript, collagen along with other elements of the ECM can regulate tumour progression and we believe our work adds an additional facet to this.

Related to the above: How were the stellate cells used for the matrisome analysis grown? In the suspension setup or adherent? This will have a large impact on the outcome. Is there for instance hyaluronic acid in this matrix?

The matrisome analysis was conducted on cells cultured in 2D. Vitamin C was added to the media to promote matrix production. We agree that this is not truly reflective of the in vivo situation but as a discovery tool this led us to identify the ADAMTS2 and ADAMTS14 substrates responsible for the function observed in 3D.

1. Performing the species-specific transcript analysis both ways is a neat approach, but why did the authors ignore the opportunity to formally overlay/compare the two stromal gene sets to define likely candidates based on statistics?

We primarily used this approach as a discovery tool to identify key differences between cancer and stellate cell compartments. Comparing the two species data sets is problematic as the murine cancer cells express many elements found in the stellate cells, while the human data set presents a cleaner comparison. This is evident from comparing metzincin expression in the two data sets. The human data set (Figure 2A) shows clear separation between cancer and stellate compartments, which is less evident in the murine data set (Supp figure 2A). As noted in supplementary figure 1A, unlike the human cancer cells used in this study, the murine cancer cells are capable of invading without stellate support (although when cultured with stellate cells invasive projections are always stellate led). Nevertheless the murine data set matches the human, although with less clarity.

Minor comments: The bioinformatics Methods need more details on how reads were mapped to the different genomes. How many mismatches were allowed and was the mapping done separately or using for instance Xenofilter?

We have improved the methodology section to include more detail for this separation. Using STAR aligner, reads were mapped to host species using a combined human and mouse genome. Ambiguous reads were subsequently discarded from the analysis. While there are bioinformatic packages that seek to match ambiguous reads to parent species we did not use these for our analysis.

The authors use the knowledge on the activities of both ADAMTS2 and -14 on collagen as a rationale to choose these two. Is there really a need for the paragraph (and associated figures) from line 102 on?

Given the prominent role collagen has been shown to have in regulating PDAC progression and the primary role for ADAMTS2 and ADAMTS14 being collagen processing, we initially hypothesised that the divergent role for these enzymes on invasion could be due to differences in collagen processing in this context. The fact that both equally contribute to collagen processing is surprising and adds to the novelty of our findings that these enzymes have a more complex role in regulating stromal biology.

We have altered the structure of the manuscript to emphasise this point. The divergent roles of ADAMTS2 and ADAMTS14 on invasion are now presented in Figure 2, with their equal role in collagen processing now presented after in Figure 3. Figure 4 onwards now details the opposing roles of these enzymes in myofibroblast differentiation and our investigation into the enzyme-specific substrates responsible for this.

Abstract, line 21; some words are missing?

We thank the reviewer for bringing this to our attention and have now amended the abstract.

Were the siRNA screen hits validated?

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Yes, hits relevant for our further investigations, MMP1 and Fibulin2, are presented in the manuscript.

What is the genotype of the mouse cancer cells? KPC-derived?

DT6066 are KPC derived while R254 are derived from KPF mice. This has been added to the methods with relevant reference.

Reviewer #1 (Significance (Required)):

The trick of dissecting tumor from stromal signals in spheroid cocultures by RNA-Seq is a cool trick, but not new and the authors should probably cite some prior work.

We have included reference to other work where researchers have used species deconvolution to explore heterocellular interactions (Lines 68-72). However, we believe our work is one of the first to use this approach to explore cellular interactions in an in vitro, 3D, invasive context.

What this all means for patients (or in vivo tumors even) remains unclear. There is some debate on whether highly activated CAFs (ACTA2/aSMA+ cells, some call them myCAFs) are indeed tumor-restrictive or whether they promote invasion. The authors appear to argue the latter (which I can agree with) but without any translational work to show what the net outcome of this mechanism is, the study remains descriptive and perhaps of limited interest.

We contend that our 3D invasion model is a powerful tool to understand the role of stellate cells in leading invasion. We have shown the utility of this model in several studies to dissect the biology of this cell type, revealing the importance of the nuclear translocation of FGFR1 in stellate invasion (PMID: 36357571), the role of the kinase PKN2 in regulating stellate heterogeneity (PMID: 35081338) and the influence of cancer cell-derived exosomes on stellate invasion (PMID: 33592190).

CAFs within PDAC stroma are highly plastic and can adopt multiple functions depending on distinct environmental cues. Thus, identifying how they are regulated is of paramount importance if they are to be therapeutically targeted. We contend that our mechanistic studies using heterocellular 3D models can aid in the dissection of the biology of these cells with more granularity than offered by clinical or in vivo studies, particularly in the context of secreted proteases. To add clinical relevance for our findings we have compared our chimera data set with previously published laser microdissected tumour and stroma PDAC tissue (Figure 2B), and identified ADAMTS2 and ADAMTS14 expression in prominent CAF subtypes (inflammatory and myofibroblastic) from published single cell RNA seq data taken from tumours (Supp figure 2C). As these enzymes are produced in multiple CAF subtypes, genetically targeting them in vivo appears prohibitive. The generation of ADAMTS2 and ADAMTS14 specific inhibitors would be required to assess their roles in vivo.

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

The manuscript by Carter and colleagues examines that role of cancer-associated fibroblasts (CAFs) in regulation of invasion in a 3D co-culture assay with epithelial cells. The authors propose that invasive chains of cancer cells are led by fibroblasts. The authors utilise a system of co-culture to create chimeric human-mouse fibroblast-cancer cell spheroids (both directions utilised, to eliminate species bias) to allow for in situ sequencing of the co-operating transcriptional programmes of each cell type during 3D invasion. From this powerful approach, this allowed the authors to identify two key two collagen-processing enzymes, ADAMTS2 and ADAMTS14, as contributing to CAF function in their system. The authors identify that these two enzymes have opposing roles in invasion, and map some of their key substrates in invasion, which extend beyond collagen-processing. The authors propose that one key function is to control the processing of TGFbeta, the latter of which is a regulator of the myofibroblast subpopulation of CAF. Overall, the findings of the manuscript are interesting, but need some further proof-of-principal demonstrations to extend their findings to support the claims within.

• The authors demonstrate a clear role of ADAMTS2 and ADAMTS14 in stellate function during differentiation and invasion. Is there any evidence of such changes in patient materials? Could the authors query publicly available databases of micro-dissected stroma vs epithelium to validate the translational relevance of their findings?

We thank the reviewer for their suggestion; we have now explored clinical relevance of ADAMTS2 and ADAMTS14 expression in two ways. We have used previously published work by Maurer and colleagues (PMID: 30658994), which descibes transcriptomic analysis of laser microdissected tumour and stroma from pancreatic cancer tissue. In accordance with our chimeric data set the majority of metzincins, including ADAMTS2 and ADAMTS14, are expressed in the sromal compartment (Figure 2B). We have also used publically available scRNA seq data to examine ADAMTS2 and ADAMTS14 expression in distinct CAF subtypes (Supp Figure 2C). Both ADAMTS2 and ADAMTS14 are expressed in inflammatory and myofibroblastic CAFs, with ADAMTS14 expression lower than that of ADAMTS2. Given the complexity of CAF heterogeneity it is possible that ADAMTS2/14 secretion by one population regulates the resulting phenotype of surrounding CAFs, however this hypothesis if beyond the scope of our current work.

Major comments: - Page no. 4, Line 71, The authors conclude that the invasion in the chimeric spheroids is "led by" stellate cells. This is a key concept in the manuscript. How do the authors define the "led by" phenomena? What is the frequency that this occurs?

In our experience all invasive projections are stellate led, defined as a stellate-labelled nucleus present at the tip of invasive projections. Indeed the human cancer cells used in this study are incapable of invading in the absence of stellate cells (Supp figure 1 A). We have previously reported this model where we demonstrated FGFR1 activity in the stellate cells is crucial for invasion (PMID: 36357571). Others have demonstrated the general importance for fibroblasts in leading invasion (PMID: 18037882, 28218910). Interestingly in our study, mouse cancer cells were capable of invading in the absence of stellate cells. However, when cultured with stellate cells, projections were predominantly stellate led.

• For Figure 2A and S2A, the text suggests that the heatmap represents the stellate vs cancer cell expression (as shown in Figure 1B and S1B) in the respective species but the labelling below the heatmap suggests they are all cancer cells (Mia, Pan, R2 and DT). Is this a typo? Could the authors clarify this?

We use Mia, Pan, R2 and DT to define the sphere combination from which the data originated. We have improved the clarity of the heatmaps by colour coding the different cell types within each sphere, and matching it with the cell type data presented in the heat map. We hope this improved labelling makes the heatmaps more accessible.

• The text and the figures are lacking information about the cell line names used in the experiment, e.g, Figure 2C, 2D, 2SB, 2SC and 2SD does not indicate what cell line was used in the study. This is the same with other figures as well. Please indicate in all instances exactly which samples are queried.

We have now included reference to the cell type and stellate cell species used in each experiment in relevant figure legends. Key 3D invasive experiments were conducted with both human and mouse stellate cells.

• It's mentioned in the text that the authors have used the cancer and stellate cells in a 1:2 ratio but the numbers of stellate cells look different between different spheroids confocal images. e.g. The numbers look very different between the Miapaca2:PS1 vs Miapaca2:mPSC spheroids. Is this simply the representative images, or are their bona fide differences. This, in turn, would impact on claims of cells being 'led' by stellate cells. Can the authors clarify?

This is a consequence of the method by which the stellate cells were immortalised. Human PS1 stellate cells were immortalised with hTERT, while mouse stellate cells were immortalised with SV40. A consequence of this is that the mouse stellate cells proliferate faster in 3D than the human stellate cells, with both proliferating slower than the cancer cell compartment. So while spheroids start at 1000 cells (666 stellate, 333 cancer) with stellate cells as the prominent component they are quickly overtaken by the cancer cells. Despite this difference in proliferation we find no difference in the invasive capacity of the stellate cells, with invasive projections always stellate led irrespective of whether they are human or mouse.

• While for most of the experiments the authors generated the chimeric spheroids first and then performed the respective experiments, it appears that for the invasion assay simply co-culture of Cancer cells and stellate cells was done. Is this correct? Have the authors tried performing the assay with the chimeric spheroids to see if the stellate cells still invade?

The Boyden chamber migration assay was conducted by seeding a co-culture of stellate and cancer cells in the apical compartment then imaging their migration to the basolateral side. This provided a second method to predominantly showcase the enhanced migration of cells lacking ADAMTS14 in a manner that could be quantified over time. We have not tried placing spheroids in the apical compartment and imaging invasion through the pores.

• The authors claim that ADAMTS2 and ADAMTS14 regulate the bioavailability of TGFB, and this is a key reason that these regulate CAF differentiation. However, there is no direct demonstration of this concept, which is conspicuous by absence. Could the authors either directly demonstrate this, or remove such notions from the results, and explicitly state that this is an untested speculation in discussion? Examples of this are:

o Line 173, authors state "ADAMTS2 facilitates TGFβ release through degradation of the plasmin inhibitor, SERPINE2 (Figure 5D)"

o Line 196 authors conclude "Together these data implicate 197 ADAMTS14 as a key regulator of TGFβ bioavailability (Figure 6F)."

o Line 240 states "This reduces the activation of Plasmin, preventing the release of TGFβ (Figure 5C)." Since this is just a model without detailed experiments, It will be better to propose rather than conclude.

We appreciate the reviewer’s concern and have now added additional experiments to strengthen the association of ADAMTS enzymes and TGFβ bioavailability.

Using a TGFβ-responsive luciferase reporter we demonstrate that the media from stellate cells lacking ADAMTS14 has greatly increased amounts of active TGFβ (Figure 4), which is abrogated when Fibulin2 is knocked down alongside (Figure 7). This links ADAMTS14 and Fibulin2 to TGFβ activity. Given the extensive literature detailing a role for Fibulin2 in regulating matrix TGFβ release through interactions with fibrillin (e.g, PMID: 19349279, 12598898, 12429738) we believe this is how ADAMTS14 is regulating myofibroblast differentiation. As we do not directly examine the association of Fibulin2 with fibrillin in this manuscript we have amended the associated statements to reflect this.

We have also used a TGFβ-responsive fluorescent reporter to examine TGFβ activity of stellate cells in 3D. Consistent with our results, loss of ADAMTS2 reduces, while loss of ADAMTS14 enhances, TGFβ activity (Figure 4), which can be reversed with concomitant knockdown of their respective substrates SERPINE2 (Figure 6) and Fibulin2 (Figure 7).

• Figure S5C shows a less invasive phenotype in the NTCsi + ADAMTS14si spheroids compared to the NTCsi + NTCsi control. However, there appears no appreciable difference between NTCsi + ADAMTS14si and NTCsi + NTCsi spheroids' brightfield images in Figure 5SD.

Could the authors comment on this?

We thank the reviewer for bringing this to our attention and apologise for our mistake. The images were positioned erroneously. This has now been corrected and the images reflect the quantification that demonstrates a clear increase in invasion following loss of ADAMTS14, which is abrogated with co-knockdown of Fibulin2.

Minor Comments: - Page no. 2, Line 20 has an incomplete sentence "Crosstalk between cancer and stellate cells is pivotal in pancreatic cancer, resulting in differentiation 21 of stellate cells into myofibroblasts that drive."

Apologies for the error. This has been rectified.

• Figure 2C; Figure S2C and Figure S5E lack quantification for the western blots.

We have now included densitometry for all western blots, presenting values relative to the respective loading control and normalised to the experimental control. Values are averages taken from all biological repeats with significance indicated where relevant.

• Why did the authors choose to investigate the Metzincin family? Could the authors provide their reasoning to investigate these proteins, to the exclusion of other candidates?

We focused on the metzincin family, as they are best known for their involvement in cancer invasion. A goal for this manuscript is to present our chimera data set as a discovery tool for the community. While this initial manuscript focuses on protease activity, we have further projects on-going that have used this data set to identify important elements of cancer/stellate communication.

• Info about the number of fields imaged per sample for the microscopy data is missing in the figure legends (e.g. Figure 2F and 2I, Figure 5SF).

We have now included a statement in each relevant figure legend to indicate that quantification was performed on at least five fields of view per biological repeat.

• Any particular reason why the ADAMTS2 expression was not checked through Western blotting like ADAMTS14 in Figure S2B.

We attempted to examine ADAMTS2 by western blotting but were unable to find an antibody that produced consistent results with our samples, and corroborated consistent knockdown by PCR.

• The legends for Figure 3SC and 5SF mention that "Images are representative of at least two biological replicates". How many technical replicates were used? It would be useful if the relative intensity of the images is measured and plotted in a graph.

We have now moved these images to the main figure alongside quantification of αSMA intensity. Images are collected from two biological repeats with quantification obtained from at least five fields of view per image. Together these data strongly demonstrate that loss of ADAMTS14 increases αSMA fibre intensity, which is blocked by either an inhibitor of TGFβ signalling (Figure 4), or co-knockdown of Fibulin2 (Figure 7).

Reviewer #2 (Significance (Required)):

This work provides an examination of the cross talk between fibroblasts and cancer cells in a 3-Dimensional culture model of pancreatic tumour cell invasion. By using chimeric human-mouse spheroids, the authors are able to identify cell-type specific transcripts by bulk RNA sequencing in situ. This advance is not to be underestimated as a number of existing approaches for cell type-specific profiling (eg. single-cell sequencing) relies upon dissociation of cell communities prior to sequencing. It is very likely that transcriptional programmes change during this isolation process. This approach allows the authors to identify transcriptional co-operating programmes in situ. This data provides a resource to understand this key co-operation of these two cell types during tumourigenesis, and will be of interest to the pancreatic cancer field. In addition, the mapping of the key substrate of these enzymes provides further insights that may be useful in understanding the expanded target repertoire of these enzymes beyond collagen processing.

We thank the reviewer for their strong support of our chimeric spheroid approach and resulting investigation into the dichotomic roles of ADAMTS2 and ADAMTS14.

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

AMADTS2 and ADAMTS14 belong to the disintegrin and metalloproteinase with thrombospondin motif protein family, mainly produced by pancreatic stellate cells (PSC) and are related to cancer cell invasion. This study reveals that ADAMTS2 and ADAMTS14 have opposite roles in myofibroblast differentiation based on experiments testing HSC driven cancer cell invasion, variant expression of HSC activation makers and the related downstream targets analysed upon RNA sequencing analyses. The authors (TA) established PSC/cancer cell chimeric spheroids for investigating the crosstalk between these cell types in 3D in vitro. Based on their findings, they claim that ADAMTS2 and ADAMTS14 have different functions regarding PSC and TGF-β activation. However, their conclusions mainly rely on quantitatve data of invasion and mechanistic details are completely lacking.

Comments: Typos, even in the abstract, e.g. first sentence incomplete

We apologise for the error in the abstract and have rectified this in the revised manuscript.

Introduction is rather sparce with one third of the text repeating the results of the study

Our manuscript details a discovery experiment using chimeric spheroids to identify cancer cell and stellate cell transcriptomes in a 3D invasive context. We then showcase the power of this data set by using it to identify and then describe divergent roles for ADAMTS2 and ADAMTS14 in shaping stellate cell biology. Given this two-tiered approach we incorporated text that would normally be placed in the introduction into the results section (e.g. our description of the importance of collagen processing in PDAC, presented as a prelude to the results from figure 3). We feel this improves the flow of the manuscript, rather than having information that isn’t necessarily relevant to the reader at the outset.

Some citations do not at all fit with the position where they are placed; needs approval

We have examined this in detail and are confident in our use of appropriate references throughout.

In this study, it is said that TS2 (AMADTS2) and TS14 (ADAMTS14) have opposite functions on myofibroblast differentiation, with individual depletion leading to distinct matrisomal phenotypes in PSC. However, both similarly contribute to collagen processing. As we know, collagen is increased in response to TGFβ signaling, since TS2 depletion (knock down, kd) inhibits and TS14 kd is suggested to promote TGFβ activation, it is expected that this has impact on the available collagen levels. How do the authors explain that nevertheless the kd effect on collagen is very similar?

The primary effects of these enzymes are on the processing of pro-collagen to its mature form, rather than on the production of collagen. This is evidenced in figure 3B where collagen expression in the whole cell lysate is the same following ADAMTS2 knockdown, and slightly reduced with loss of ADAMTS14, but the mature form is lost in the cell culture supernatant.

While myofibroblast differentiation is associated with increased collagen production, it is possible that this is perturbed in a situation where the cell is surrounded by collagen that is incompletely processed (e.g. through biomechanical feedback). Given that our results clearly indicated that the effect of ADAMTS2 and ADAMTS14 on invasion is independent of their roles in collagen processing, this avenue is beyond the scope of the current manuscript.

The authors claim that TS2 facilitates TGFβ release and TS14 is a key regulator of TGFβ bioavailability. However, throughout the whole data, there is no experimental evidence for this conclusion. TGFβ activation, LAP concentration and downstream effects should be provided.

Most of the conclusions in the manuscript are based on effects to invasion and the estimated quantification histograms. "Black boxes in between the treatment, e.g. knockdown and readout, that relate to the signals and mechanisms remain black boxes throughout. For example, the impact of the treatments on stellate cell activation markers, the cancer cells invasion signaling, the SERPINE2- and Fibulin2-dependent myofibroblast differentiation pathways should be mechanistically investigated.

We disagree with this comment. Our invasive model shows a clear role for ADAMTS2 and ADAMTS14 in regulating invasion, which is mitigated by disrupting their substrates SERPINE2 and Fibulin2.

ADAMTS2 loss is associated with a reduction in plasmin activity, which again is mitigated with concurrent loss of SERPINE2. Equally, inhibition of plasmin activity with Aprotinin matches the loss of invasion observed with loss of ADAMTS2. Plasmin has a well-established role in mediating TGFβ release from the matrix. We have now included additional experiments using a TGFβ fluorescent reporter in 3D culture. This demonstrates that loss of ADAMTS2 reduces TGFβ activity, which can be rescued with co-knockdown of SERPINE2 (Figure 6). Our data therefore support a mechanism where ADAMTS2 blocks TGFβ release from the matrix, and therefore myofibroblast differentiation, through its regulation of SERPINE2 activity.

We have strengthened our proposed mechanism for ADAMTS14 regulation of TGFβ through Fibulin2 with the use of both luciferase and fluorescent TGFβ reporter constructs. Using these reporters, we demonstrate that stellate cells lacking ADAMTS14 exhibit increased TGFβ activity (Figure 4), which is mitigated with co-knockdown of Fibulin2 (Figure 7). Combined with the effects on αSMA expression and 3D invasion, our data fit with a model where ADAMTS14 regulates TGFβ bioavailability through Fibulin2.

The authors investigate one cell line each for their conclusions; we know that different cell lines behave differently; can they confirm that the finding they present is of general validity or a finding that is specific for the tested cancer/PSC cell lines. Can the principle findings also be proven in primary cells. More importantly, the authors should proof their findings in PaCa tissue of patients as follows: Expression of the proteases in the tissue, related variation of matrisome signatures, e.g. by snRNASeq, to confirm relevance of the finding.

All our key 3D invasive experiments are repeated with both human and mouse stellate cells, adding strength to our proposed association with ADAMTS2 and SERPINE2, and ADAMTS14 and Fibulin2, on the invasive capacity of stellate cells. As detailed above we have explored the clinical relevance of our findings by examining laser dissected tumour and stromal data from PDAC tissue, and scRNA fibroblast data. These data confirm that ADAMTS2 and ADAMTS14 are predominantly expressed in the stromal compartment of the tumour and are associated with key CAF subtypes present in the PDAC environment, inflammatory and myofibroblastic CAFs.

Details related to the figures: Figure 1: Are the numbers of PSC and PaCa cells integrated in the spheres related to the numbers found in patients?

The 2:1 ratio of stellate to cancer cells used to produce spheres is a technical requirement and reflects the numbers in patients (PMID: 23359139). Cancer cells will proliferate substantially faster than the stellate cells so at the end of the experiment (day 3) the spheres are predominantly cancer cells. Nevertheless the stellate cells are able to drive invasion of the cancer cells, which can be quantitatively assessed in this model.

B, it seems that the PSC in the spheroid are not equally distributed but instead are all located in close vicinity to eachother in a cloud; is that the representative situation for the spheres and is this similar in the PaCa cancer tissue? Does this have influence on the results?

We have replaced this image with a more representative image that shows mouse stellate cells dispersed throughout the sphere.

Figure 2: It is interesting to hear that BMP1, which is actually a ligand for BMP signaling is a protease for Collagen. How does this work?

While the BMP family generally belong to the TGFβ superfamily, BMP1 is the exception in that it is a C-terminal collagenase. Please refer to reference 21 in the manuscript (PMID: 33879793), which details the role of BMP1 on collagen processing and the resulting effect on PDAC progression.

C, Quantification of all blots should be presented.

We have now included densitometry for all western blots, presenting values relative to the loading control and normalised to the experimental control. Values are averages taken from all biological repeats with significance indicated by stars.

Figure S2: TS2 kd and TS14 kd should be confirmed and provided by both qrt PCR and WB data.

We were unable to assess ADAMTS2 knockdown by western blot due to the quality of available antibodies. We are confident that either western or PCR confirmation of knockdown is sufficient, especially given the strong phenotype observed with the resulting knockdown.

Figure 3: F; this result is arguing against the conclusion that TGFb bioavailability is a function of the ADAMs, since the kd impacts on the treatment result with exogenous TGFb. This suggests an effect downstream of ligand activation by proteasomal cleavage, e.g. receptor activation or signal transduction; this needs clarification. H, I: TGFβR inhibitor reduces TS14kd enhanced αSMA expression. How is unclear and needs clarification, since from F we know that already activated TGFβ needs TS2 to fully induce αSMA expression.

SupplFig.3: B, C, as above!

αSMA expression in stellate cells requires continuous exposure to TGFβ over 48 hours. Active TGFβ has an incredibly short half-life (minutes) and so requires positive feedback to maintain signalling. We propose that following ADAMTS2 knockdown the cells are incapable of releasing further TGFβ to maintain the phenotype. Equally following ADAMTS14 knockdown the cells are able to release more TGFβ, which is incapable of initiating signalling when the receptor is blocked.

Figure 4: TIMP1 is a canonical TGFb signaling target gene in fibrosis. How the authors explain that TIMP1 is upregulated in both knockdowns, when they claim that TS2 and 14 have opposing functions on TGFb activation. This result as well puts their conclusions as regards TGFb and also the myofibroblast phenotype into question. Especially, since TIMP1 signifies stellate cell activation not only in the pancreas, but also in the liver and kidney. C, D, E should be explained in more detail and all details of the results should be presented.

TIMP1 is a substrate for both ADAMTS2 and ADAMTS14, so its enrichment following knockdown of either is unsurprising, reflective of reduced cleavage of TIMP1. Both our 3D invasive assessment in Figure 6 and αSMA imaging in supplementary figure 5 demonstrate that TIMP1 is not responsible for the effect observed as a consequence from loss of either ADAMTS2 or ADAMTS14.

This holds also for the different myofibroblast phenotypes. All data should be included. From recent scRNASeq investigations, several myofibroblast populations were described and compared, e.g my-stellate cells vs i-stellate cells. To which of these phenotypes the identified populations belong?

As mentioned above, we have interrogated publically available data sets and identified ADAMTS2 and ADAMTS14 expression in multiple CAF subtypes. As these proteases are secreted it is probable that one CAF subtype can control the phenotype of surrounding CAFs through ADAMTS2 and ADAMTS14 production. While intriguing, this hypotheses is beyond the scope of the current work.

Figure 5: C, Only brightfield images are provided, confocal images are suggested for comparison of +/- Aprotinin treatment.

We do not think the addition of confocal images will add to the comparison. Aprotinin clearly reduces invasion, which coupled with the action of stellate-derived SERPINE2 on invasion, and reduced plasmin activity following ADAMTS2 knockdown, suggests that plasmin is important for regulating the effects of ADAMTS2 on invasion.

The efficiency of TS2 and Serpine2 kd should be provided by qrt PCR and WB.

TS2 kd promoted SERPINE2 expression should also be presented by qrt PCR and WB.

We are confident that either western or PCR confirmation of knockdown is sufficient. Of note is that following ADAMTS2 knockdown, SERPINE2 expression is unchanged (sup figure 4C). This would indicate that the enrichment of SERPINE2 observed in the matrisome following loss of ADAMTS2 is reflective of reduced cleavage, rather than a change in expression.

Figure 6: A, why ta use aSMA and not invasive activity as a readout here?

Increased αSMA expression following ADAMTS14 knockdown provides a strong, clear, 2D phenotype to act as a readout for an siRNA screen with high-content imaging. Performing such a screen with our 3D invasive model is currently impractical.

There are many parameters leading to decreased aSMA expression upon kd; (1) why only MMP1 and Fibulin were selected as candidates?

From our αSMA screen, MMP1 and Fibulin2 knockdown were the only candidates that were able to both prevent an increase in αSMA seen with ADAMTS14 loss alone, and are known ADAMTS14 substrates. Further validation in our 3D invasive model demonstrated that Fibulin2 and not MMP1 was responsible for the effect of ADAMTS14 loss on invasion.

(2) the single kd control of the screen candidates is missing!

We feel this control is not needed, as the goal of the experiment was to establish which candidate was responsible for mediating the effects brought about by ADAMTS14 knockdown. Increased αSMA expression with IL-1β loss validates our approach, as this is a known negative regulator of TGFβ signalling.

(3) Can it be expected that all these matrisomal proteins are involved in aSMA expression regulation? I have doubts.

We agree with the reviewers comment, from the siRNA screen (sup figure 5B) it is clear that the majority of the identified matrisome proteins have a minimal effect on αSMA expression following loss of ADAMTS14.

C, D, E, why MMP1 was not also tested in these assays?

Our spheroid assay clearly demonstrated that invasion was enhanced following ADAMTS14 knockdown even with co-knockdown of MMP1. Given the strong rescue observed with co-knockdown of Fibulin2 we proceeded to further analyse this candidate over MMP1.

F, Fibrillin is shown in the figure but not described in the text. It would be quite interesting to see whether Fibrillin kd has the same effect as TS14 kd on LTGF-β activation (which of course need to be shown experimentally).

The association of fibrillin with TGFβ release is well established as it underpins the biology behind Marfan syndrome. Loss of fibrillin, or mutations to its TGFβ binding sites results in a phenotype consistent with super active TGFβ signalling.

E, what is the meaning of αSMA intensity quantification? By IF staining of αSMA? PSC αSMA expression should be quantified by qrt PCR and WB.

We have now incorporated the confocal images analysing αSMA expression into the main figure and labelled the quantification accordingly. We feel this improves the clarity of the figures. Every western blot is now presented with quantification.

Also here, kd efficiency of TS14 and Fibulin2 should be provided by qrt PCR and WB.

Figure S5E should be part of figure 6, qrt PCR of Fibulin2 should be added.

We have moved this western blot to the main figure (Fig 7C). We feel additional PCR validation of Fibulin 2 knockdown is not necessary.

Figure 5/6 and throughout: It is claimed that ADAMTS2 and ADAMTS14 regulate TGFβ bioavailability through SREPINE2-Plasmin and Fibulin2. As mentioned above, TGFβ activation is only mentioned in the schemes, but no experimental evidence is given. In addition, according to previous studies, ADAMTSs can activate latent TGFβ directly by interaction with the LAP of latent TGFβ. .

We have now included extra experimental evidence to support an association of ADAMTS proteins with TGFβ bioavailability. Using a TGFβ luciferase reporter construct, we demonstrate that active TGFβ is increased following loss of ADAMTS14, which is abrogated with concomitant loss of Fibulin2. This provides further evidence that ADAMTS14 is mediating its effects on myofibroblast differentiation / invasion through TGFβ release.

Figure 3B, C, and 6D: We are confused from the migration/invasion assays. Invasion should be based on migration of tumor cells, whereas in the migration assays only stellate cells seem to be active? Can you explain this to us? According to Figure 3B, stellate and cancer cells are cocultured in the chamber. Is this the same condition as for the experiment presented as figure 6D?

In our migration assay, stellate and cancer cells are co-cultured in the apical chamber and cell migration imaged over time. We pooled data of both cancer and stellate cell migration following stellate specific knockdown of either ADAMTS2 or ADAMTS14, which showed an increase in cell migration following loss of ADAMTS14. In figure 7, we again use this assay to demonstrate that Fibulin2 expression accounts for the phenotype observed from loss of ADAMTS14.

In summary, this study for the first time found that ADAMTS2 and ADAMTS14 have opposite roles on myofibroblast differentiation, which is shown by using chimeric spheroids of stellate and pancreatic cancer cells. The authors claim a therapeutic potential for pancreatic cancer by regulating ADAMTS2/14-mediated stellate cell activation, which should avoid cancer cell invasion. The approach is interesting and there is preliminary evidence, however the study has many gaps and requires substantive workload.

We thank the reviewer for their support of our findings. We hope the additional data, combined with the known role for these substrates in the regulation of TGFβ, strengthens the clarity of 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

AMADTS2 and ADAMTS14 belong to the disintegrin and metalloproteinase with thrombospondin motif protein family, mainly produced by pancreatic stellate cells (PSC) and are related to cancer cell invasion. This study reveals that ADAMTS2 and ADAMTS14 have opposite roles in myofibroblast differentiation based on experiments testing HSC driven cancer cell invasion, variant expression of HSC activation makers and the related downstream targets analysed upon RNA sequencing analyses. The authors (TA) established PSC/cancer cell chimeric spheroids for investigating the crosstalk between these cell types in 3D in vitro. Based on their findings, they claim that ADAMTS2 and ADAMTS14 have different functions regarding PSC and TGF-β activation. However, their conclusions mainly rely on quantitatve data of invasion and mechanistic details are completely lacking.

Comments:

Typos, even in the abstract, e.g. first sentence incomplete Introduction is rather sparce with one third of the text repeating the results of the study Some citations do not at all fit with the position where they are placed; needs approval

In this study, it is said that TS2 (AMADTS2) and TS14 (ADAMTS14) have opposite functions on myofibroblast differentiation, with individual depletion leading to distinct matrisomal phenotypes in PSC. However, both similarly contribute to collagen processing. As we know, collagen is increased in response to TGFβ signaling, since TS2 depletion (knock down, kd) inhibits and TS14 kd is suggested to promote TGFβ activation, it is expected that this has impact on the available collagen levels. How do the authors explain that nevertheless the kd effect on collagen is very similar?

The authors claim that TS2 facilitates TGFβ release and TS14 is a key regulator of TGFβ bioavailability. However, throughout the whole data, there is no experimental evidence for this conclusion. TGFβ activation, LAP concentration and downstream effects should be provided.

Most of the conclusions in the manuscript are based on effects to invasion and the estimated quantification histograms. "Black boxes in between the treatment, e.g. knockdown and readout, that relate to the signals and mechanisms remain black boxes throughout. For example, the impact of the treatments on stellate cell activation markers, the cancer cells invasion signaling, the SERPINE2- and Fibulin2-dependent myofibroblast differentiation pathways should be mechanistically investigated.

The authors investigate one cell line each for their conclusions; we know that different cell lines behave differently; can they confirm that the finding they present is of general validity or a finding that is specific for the tested cancer/PSC cell lines. Can the principle findings also be proven in primary cells. More importantly, the authors should proof their findings in PaCa tissue of patients as follows: Expression of the proteases in the tissue, related variation of matrisome signatures, e.g. by snRNASeq, to confirm relevance of the finding.

Details related to the figures:

Figure 1: Are the numbers of PSC and PaCa cells integrated in the spheres related to the numbers found in patients? B, it seems that the PSC in the spheroid are not equally distributed but instead are all located in close vicinity to eachother in a cloud; is that the representative situation for the spheres and is this similar in the PaCa cancer tissue? Does this have influence on the results?

Figure 2: It is interesting to hear that BMP1, which is actually a ligand for BMP signaling is a protease for Collagen. How does this work? C, Quantification of all blots should be presented.

Figure S2: TS2 kd and TS14 kd should be confirmed and provided by both qrt PCR and WB data.

Figure 3: F; this result is arguing against the conclusion that TGFb bioavailability is a function of the ADAMs, since the kd impacts on the treatment result with exogenous TGFb. This suggests an effect downstream of ligand activation by proteasomal cleavage, e.g. receptor activation or signal transduction; this needs clarification. H, I: TGFβR inhibitor reduces TS14kd enhanced αSMA expression. How is unclear and needs clarification, since from F we know that already activated TGFβ needs TS2 to fully induce αSMA expression.

SupplFig.3: B, C, as above!

Figure 4: TIMP1 is a canonical TGFb signaling target gene in fibrosis. How the authors explain that TIMP1 is upregulated in both knockdowns, when they claim that TS2 and 14 have opposing functions on TGFb activation. This result as well puts their conclusions as regards TGFb and also the myofibroblast phenotype into question. Especially, since TIMP1 signifies stellate cell activation not only in the pancreas, but also in the liver and kidney. C, D, E should be explained in more detail and all details of the results should be presented. This holds also for the different myofibroblast phenotypes. All data should be included. From recent scRNASeq investigations, several myofibroblast populations were described and compared, e.g my-stellate cells vs i-stellate cells. To which of these phenotypes the identified populations belong?

Figure 5: C, Only brightfield images are provided, confocal images are suggested for comparison of +/- Aprotinin treatment. The efficiency of TS2 and Serpine2 kd should be provided by qrt PCR and WB. TS2 kd promoted SERPINE2 expression should also be presented by qrt PCR and WB.

Figure 6: A, why ta use aSMA and not invasive activity as a readout here? There are many parameters leading to decreased aSMA expression upon kd; (1) why only MMP1 and Fibulin were selected as candidates? (2) the single kd control of the screen candidates is missing! (3) Can it be expected that all these matrisomal proteins are involved in aSMA expression regulation? I have doubts. C, D, E, why MMP1 was not also tested in these assays? F, Fibrillin is shown in the figure but not described in the text. It would be quite interesting to see whether Fibrillin kd has the same effect as TS14 kd on LTGF-β activation (which of course need to be shown experimentally). E, what is the meaning of αSMA intensity quantification? By IF staining of αSMA? PSC αSMA expression should be quantified by qrt PCR and WB. Also here, kd efficiency of TS14 and Fibulin2 should be provided by qrt PCR and WB.

Figure S5E should be part of figure 6, qrt PCR of Fibulin2 should be added.

Figure 5/6 and throughout: It is claimed that ADAMTS2 and ADAMTS14 regulate TGFβ bioavailability through SREPINE2-Plasmin and Fibulin2. As mentioned above, TGFβ activation is only mentioned in the schemes, but no experimental evidence is given. In addition, according to previous studies, ADAMTSs can activate latent TGFβ directly by interaction with the LAP of latent TGFβ. . Figure 3B, C, and 6D: We are confused from the migration/invasion assays. Invasion should be based on migration of tumor cells, whereas in the migration assays only stellate cells seem to be active? Can you explain this to us? According to Figure 3B, stellate and cancer cells are cocultured in the chamber. Is this the same condition as for the experiment presented as figure 6D?

In summary, this study for the first time found that ADAMTS2 and ADAMTS14 have opposite roles on myofibroblast differentiation, which is shown by using chimeric spheroids of stellate and pancreatic cancer cells. The authors claim a therapeutic potential for pancreatic cancer by regulating ADAMTS2/14-mediated stellate cell activation, which should avoid cancer cell invasion. The approach is interesting and there is preliminary evidence, however the study has many gaps and requires substantive workload.

Significance

AMADTS2 and ADAMTS14 belong to the disintegrin and metalloproteinase with thrombospondin motif protein family, mainly produced by pancreatic stellate cells (PSC) and are related to cancer cell invasion. This study reveals that ADAMTS2 and ADAMTS14 have opposite roles in myofibroblast differentiation based on experiments testing HSC driven cancer cell invasion, variant expression of HSC activation makers and the related downstream targets analysed upon RNA sequencing analyses.

The authors (TA) established PSC/cancer cell chimeric spheroids for investigating the crosstalk between these cell types in 3D in vitro. Based on their findings, they claim that ADAMTS2 and ADAMTS14 have different functions regarding PSC and TGF-β activation. However, their conclusions mainly rely on quantitatve data of invasion and mechanistic details are completely lacking.

Comments:

Typos, even in the abstract, e.g. first sentence incomplete Introduction is rather sparce with one third of the text repeating the results of the study Some citations do not at all fit with the position where they are placed; needs approval

In this study, it is said that TS2 (AMADTS2) and TS14 (ADAMTS14) have opposite functions on myofibroblast differentiation, with individual depletion leading to distinct matrisomal phenotypes in PSC. However, both similarly contribute to collagen processing. As we know, collagen is increased in response to TGFβ signaling, since TS2 depletion (knock down, kd) inhibits and TS14 kd is suggested to promote TGFβ activation, it is expected that this has impact on the available collagen levels. How do the authors explain that nevertheless the kd effect on collagen is very similar?

The authors claim that TS2 facilitates TGFβ release and TS14 is a key regulator of TGFβ bioavailability. However, throughout the whole data, there is no experimental evidence for this conclusion. TGFβ activation, LAP concentration and downstream effects should be provided.

Most of the conclusions in the manuscript are based on effects to invasion and the estimated quantification histograms. "Black boxes in between the treatment, e.g. knockdown and readout, that relate to the signals and mechanisms remain black boxes throughout. For example, the impact of the treatments on stellate cell activation markers, the cancer cells invasion signaling, the SERPINE2- and Fibulin2-dependent myofibroblast differentiation pathways should be mechanistically investigated.

The authors investigate one cell line each for their conclusions; we know that different cell lines behave differently; can they confirm that the finding they present is of general validity or a finding that is specific for the tested cancer/PSC cell lines. Can the principle findings also be proven in primary cells. More importantly, the authors should proof their findings in PaCa tissue of patients as follows: Expression of the proteases in the tissue, related variation of matrisome signatures, e.g. by snRNASeq, to confirm relevance of the finding.

Details related to the figures:

Figure 1: Are the numbers of PSC and PaCa cells integrated in the spheres related to the numbers found in patients? B, it seems that the PSC in the spheroid are not equally distributed but instead are all located in close vicinity to eachother in a cloud; is that the representative situation for the spheres and is this similar in the PaCa cancer tissue? Does this have influence on the results?

Figure 2: It is interesting to hear that BMP1, which is actually a ligand for BMP signaling is a protease for Collagen. How does this work? C, Quantification of all blots should be presented.

Figure S2: TS2 kd and TS14 kd should be confirmed and provided by both qrt PCR and WB data.

Figure 3: F; this result is arguing against the conclusion that TGFb bioavailability is a function of the ADAMs, since the kd impacts on the treatment result with exogenous TGFb. This suggests an effect downstream of ligand activation by proteasomal cleavage, e.g. receptor activation or signal transduction; this needs clarification. H, I: TGFβR inhibitor reduces TS14kd enhanced αSMA expression. How is unclear and needs clarification, since from F we know that already activated TGFβ needs TS2 to fully induce αSMA expression.

SupplFig.3: B, C, as above!

Figure 4: TIMP1 is a canonical TGFb signaling target gene in fibrosis. How the authors explain that TIMP1 is upregulated in both knockdowns, when they claim that TS2 and 14 have opposing functions on TGFb activation. This result as well puts their conclusions as regards TGFb and also the myofibroblast phenotype into question. Especially, since TIMP1 signifies stellate cell activation not only in the pancreas, but also in the liver and kidney. C, D, E should be explained in more detail and all details of the results should be presented. This holds also for the different myofibroblast phenotypes. All data should be included. From recent scRNASeq investigations, several myofibroblast populations were described and compared, e.g my-stellate cells vs i-stellate cells. To which of these phenotypes the identified populations belong?

Figure 5: C, Only brightfield images are provided, confocal images are suggested for comparison of +/- Aprotinin treatment. The efficiency of TS2 and Serpine2 kd should be provided by qrt PCR and WB. TS2 kd promoted SERPINE2 expression should also be presented by qrt PCR and WB.

Figure 6: A, why ta use aSMA and not invasive activity as a readout here? There are many parameters leading to decreased aSMA expression upon kd; (1) why only MMP1 and Fibulin were selected as candidates? (2) the single kd control of the screen candidates is missing! (3) Can it be expected that all these matrisomal proteins are involved in aSMA expression regulation? I have doubts. C, D, E, why MMP1 was not also tested in these assays? F, Fibrillin is shown in the figure but not described in the text. It would be quite interesting to see whether Fibrillin kd has the same effect as TS14 kd on LTGF-β activation (which of course need to be shown experimentally). E, what is the meaning of αSMA intensity quantification? By IF staining of αSMA? PSC αSMA expression should be quantified by qrt PCR and WB. Also here, kd efficiency of TS14 and Fibulin2 should be provided by qrt PCR and WB.

Figure S5E should be part of figure 6, qrt PCR of Fibulin2 should be added.

Figure 5/6 and throughout: It is claimed that ADAMTS2 and ADAMTS14 regulate TGFβ bioavailability through SREPINE2-Plasmin and Fibulin2. As mentioned above, TGFβ activation is only mentioned in the schemes, but no experimental evidence is given. In addition, according to previous studies, ADAMTSs can activate latent TGFβ directly by interaction with the LAP of latent TGFβ. .

Figure 3B, C, and 6D: We are confused from the migration/invasion assays. Invasion should be based on migration of tumor cells, whereas in the migration assays only stellate cells seem to be active? Can you explain this to us? According to Figure 3B, stellate and cancer cells are cocultured in the chamber. Is this the same condition as for the experiment presented as figure 6D?

In summary, this study for the first time found that ADAMTS2 and ADAMTS14 have opposite roles on myofibroblast differentiation, which is shown by using chimeric spheroids of stellate and pancreatic cancer cells. The authors claim a therapeutic potential for pancreatic cancer by regulating ADAMTS2/14-mediated stellate cell activation, which should avoid cancer cell invasion. The approach is interesting and there is preliminary evidence, however the study has many gaps and requires substantive workload.

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Carter and colleagues examines that role of cancer-associated fibroblasts (CAFs) in regulation of invasion in a 3D co-culture assay with epithelial cells. The authors propose that invasive chains of cancer cells are led by fibroblasts. The authors utilise a system of co-culture to create chimeric human-mouse fibroblast-cancer cell spheroids (both directions utilised, to eliminate species bias) to allow for in situ sequencing of the co-operating transcriptional programmes of each cell type during 3D invasion. From this powerful approach, this allowed the authors to identify two key two collagen-processing enzymes, ADAMTS2 and ADAMTS14, as contributing to CAF function in their system. The authors identify that these two enzymes have opposing roles in invasion, and map some of their key substrates in invasion, which extend beyond collagen-processing. The authors propose that one key function is to control the processing of TGFbeta, the latter of which is a regulator of the myofibroblast subpopulation of CAF. Overall, the findings of the manuscript are interesting, but need some further proof-of-principal demonstrations to extend their findings to support the claims within.

• The authors demonstrate a clear role of ADAMTS2 and ADAMTS14 in stellate function during differentiation and invasion. Is there any evidence of such changes in patient materials? Could the authors query publicly available databases of micro-dissected stroma vs epithelium to validate the translational relevance of their findings?

Major comments:

• Page no. 4, Line 71, The authors conclude that the invasion in the chimeric spheroids is "led by" stellate cells. This is a key concept in the manuscript. How do the authors define the "led by" phenomena? What is the frequency that this occurs?
• For Figure 2A and S2A, the text suggests that the heatmap represents the stellate vs cancer cell expression (as shown in Figure 1B and S1B) in the respective species but the labelling below the heatmap suggests they are all cancer cells (Mia, Pan, R2 and DT). Is this a typo? Could the authors clarify this?
• The text and the figures are lacking information about the cell line names used in the experiment, e.g, Figure 2C, 2D, 2SB, 2SC and 2SD does not indicate what cell line was used in the study. This is the same with other figures as well. Please indicate in all instances exactly which samples are queried.
• It's mentioned in the text that the authors have used the cancer and stellate cells in a 1:2 ratio but the numbers of stellate cells look different between different spheroids confocal images. e.g. The numbers look very different between the Miapaca2:PS1 vs Miapaca2:mPSC spheroids. Is this simply the representative images, or are their bona fide differences. This, in turn, would impact on claims of cells being 'led' by stellate cells. Can the authors clarify?
• While for most of the experiments the authors generated the chimeric spheroids first and then performed the respective experiments, it appears that for the invasion assay simply co-culture of Cancer cells and stellate cells was done. Is this correct? Have the authors tried performing the assay with the chimeric spheroids to see if the stellate cells still invade?

• The authors claim that ADAMTS2 and ADAMTS14 regulate the bioavailability of TGFB, and this is a key reason that these regulate CAF differentiation. However, there is no direct demonstration of this concept, which is conspicuous by absence. Could the authors either directly demonstrate this, or remove such notions from the results, and explicitly state that this is an untested speculation in discussion? Examples of this are:

  • Line 173, authors state "ADAMTS2 facilitates TGFβ release through degradation of the plasmin inhibitor, SERPINE2 (Figure 5D)"
  • Line 196 authors conclude "Together these data implicate 197 ADAMTS14 as a key regulator of TGFβ bioavailability (Figure 6F)."
  • Line 240 states "This reduces the activation of Plasmin, preventing the release of TGFβ (Figure 5C)." Since this is just a model without detailed experiments, It will be better to propose rather than conclude.

• Figure S5C shows a less invasive phenotype in the NTCsi + ADAMTS14si spheroids compared to the NTCsi + NTCsi control. However, there appears no appreciable difference between NTCsi + ADAMTS14si and NTCsi + NTCsi spheroids' brightfield images in Figure 5SD. Could the authors comment on this?

Minor Comments:

• Page no. 2, Line 20 has an incomplete sentence "Crosstalk between cancer and stellate cells is pivotal in pancreatic cancer, resulting in differentiation 21 of stellate cells into myofibroblasts that drive."
• Figure 2C; Figure S2C and Figure S5E lack quantification for the western blots.
• Why did the authors choose to investigate the Metzincin family? Could the authors provide their reasoning to investigate these proteins, to the exclusion of other candidates?
• Info about the number of fields imaged per sample for the microscopy data is missing in the figure legends (e.g. Figure 2F and 2I, Figure 5SF).
• Any particular reason why the ADAMTS2 expression was not checked through Western blotting like ADAMTS14 in Figure S2B.
• The legends for Figure 3SC and 5SF mention that "Images are representative of at least two biological replicates". How many technical replicates were used? It would be useful if the relative intensity of the images is measured and plotted in a graph.

Significance

This work provides an examination of the cross talk between fibroblasts and cancer cells in a 3-Dimensional culture model of pancreatic tumour cell invasion. By using chimeric human-mouse spheroids, the authors are able to identify cell-type specific transcripts by bulk RNA sequencing in situ. This advance is not to be underestimated as a number of existing approaches for cell type-specific profiling (eg. single-cell sequencing) relies upon dissociation of cell communities prior to sequencing. It is very likely that transcriptional programmes change during this isolation process. This approach allows the authors to identify transcriptional co-operating programmes in situ. This data provides a resource to understand this key co-operation of these two cell types during tumourigenesis, and will be of interest to the pancreatic cancer field. In addition, the mapping of the key substrate of these enzymes provides further insights that may be useful in understanding the expanded target repertoire of these enzymes beyond collagen processing.

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Referee #1

Evidence, reproducibility and clarity

This study aims to explain the opposing contributions of stromal stellate cells/CAFs to PDAC. By first identifying stroma-specific proteases, followed by a process of candidate selection and elimination, the authors find that two specific metalloproteases that share enzymatic activity against collagen in fact have differential activity on TGFb availability. This could be interpreted as a way of shaping the CAF population and tumor-promotin or -restricting properties of the stroma.

There are several flaws that the authors could address to improve the manuscript:

1. In the flow of experiments and analyses, there is a strange mix of fully unbiased discovery phases followed by functional experiments that do not consider all possible candidates to test, and vice versa. For instance, from the mixed-species transcript analysis, ADAMTS2 and -14 are chosen based on their shared collagenase activity based on literature. However, the authors then perform again a proteomics analysis to identify things from the entire matrisome that are cleaved by these enzymes? Then, for ADAMTS2 a co-silencing approach is done on one selected candidate (Serpine2), but for ADAMTS14 an siRNA screen is performed? The problem of this approach is that the rationale for some studied enzymes is very strong, where as for others it is not.
2. The ECM is more than just collagen. Choosing these two metalloproteases based on their shared collagen substrate is an approach that perhaps oversimplifies the ECM a bit, and again, does not provide the strongest rationale that these metalloproteases are most likely to explain counteracting stromal activities on tumor growth and progression.
3. Related to the above: How were the stellate cells used for the matrisome analysis grown? In the suspension setup or adherent? This will have a large impact on the outcome. Is there for instance hyaluronic acid in this matrix?
4. Performing the species-specific transcript analysis both ways is a neat approach, but why did the authors ignore the opportunity to formally overlay/compare the two stromal gene sets to define likely candidates based on statistics?

Minor comments:

The bioinformatics Methods need more details on how reads were mapped to the different genomes. How many mismatches were allowed and was the mapping done separately or using for instance Xenofilter?

The authors use the knowledge on the activities of both ADAMTS2 and -14 on collagen as a rationale to choose these two. Is there really a need for the paragraph (and associated figures) from line 102 on?

Abstract, line 21; some words are missing?

Were the siRNA screen hits validated?

What is the genotype of the mouse cancer cells? KPC-derived?

Significance

The trick of dissecting tumor from stromal signals in spheroid cocultures by RNA-Seq is a cool trick, but not new and the authors should probably cite some prior work.

What this all means for patients (or in vivo tumors even) remains unclear. There is some debate on whether highly activated CAFs (ACTA2/aSMA+ cells, some call them myCAFs) are indeed tumor-restrictive or whether they promote invasion. The authors appear to argue the latter (which I can agree with) but without any translational work to show what the net outcome of this mechanism is, the study remains descriptive and perhaps of limited interest.

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Reply to the reviewers

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

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Referee #2

Evidence, reproducibility and clarity

This study by Kordala et al reports the identification of new therapeutics to further improve the clinical outcomes of spinal muscular atrophy (SMA) patients. SMA is childhood neurological disease that is caused by insufficient levels of the survival motor neuron (SMN) protein. There are currently three approved therapies for SMA, yet the disease is not cured and many patients remain severely disabled. The authors conducted a screen of known epigenetic regulators to identify molecules that increase SMN protein. They identified MS023, which is a selectively PRMT inhibitor, that promotes SMN exon 7 inclusion and thus full length SMN protein. Importantly, MS023 improves the SMA phenotype alone or in combination with the SMN2 antisense oligonucleotide suggesting it can potentially be used by itself or in combinatorial approaches. While this is a generally well written paper with relatively straight forward experimental design there remains some concerns that should be addressed.

Major Concerns:

1. The mechanism of action needs further clarification. Does MS023 work similarly to Risdaplam? Also, if Nusinersen is already interfering with hnRNPA1 how does MS023 augment the splicing.
2. MS023 alone did not increase improve exon 7 inclusion in the spinal cord of treated SMA mice yet the protein levels were increased (Fig. 3D,F). Are there alternative mechanisms through which MS023 is acting?
3. Further explanation of why MS023 did not improve exon 7 inclusion in the spinal cord but enhanced the effect of the ASO (Fig. 4B) is needed.
4. Nusinersen has been shown to almost completely rescue the SMA phenotype in mice. Was the dose used here chosen to be suboptimal?

Minor Concern:

Many neurological diseases are now moving to a multimodal approach. The manuscript could be improved with further discussion of why MS023 would be an attractive option compared to other synergistic strategies being employed for SMA, including the most obvious of combining some of the already approved therapies.

Significance

This is a generally well done study that works through a screening methodology to identify a molecule that increase the levels of SMN. Mechanistic studies suggest that the compound works through inhibiting the recruitment of hnRNPA1 to the SMN2 gene, thus promoting inclusion of exon 7 and the production of full-length SMN protein.

The study does not provide definitive data that methyl transferase activity of PRMT promotes exon 7 exclusion or that the inhibitor changes the methylation state of any of the proteins involved. However, knockdown experiments does not exclude this possibility.

This study would be of general interest to wider audience if more detail was included regarding the current SMA landscape and how MS023 fits in with what is currently available. The transcriptome data was potentially very interesting since it provided clues on how MS023 is exerting its synergistic effect(neuroinflammation angle is relatively unique), but that data was only briefly discussed.

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Referee #1

Evidence, reproducibility and clarity

Summary

SMA is a severe, monogenetic, progressive neuromuscular disease that mostly affects young children. SMA is cause by homozygous loss of function of SMN1. The main modifier of disease severity - that ranges widely, from neonatal to adult onset - is the presence of a varying number of SMN2 copies in the human genome. Recently, several gene-targeting therapies for SMA have been approved. This has changed the outcome of SMA drastically for many patients, but, surprisingly, the effect of these treatments varies strongly between patients. This leads to significant uncertainty for patients, families and clinicians and poses a challenge to reliable prognosis.

One of the drugs that has been approved for treating SMA is the antisense oligonucleotide nusinersen (Spinraza). Nusinersen improves SMA outcomes by enhancing the splicing of SMN2 -transcribed pre-mRNA, leading to an increase in the inclusion of exon 7 leading to an increase in the availability of full-length, functional SMN protein. In the current manuscript, Kordala and colleagues investigate the effect of a library of 54 compounds (focused on modulating epigenetic regulators) on SMN2 splicing and SMN protein in an SMA type II patient fibroblast cell line. They found the Type I PMRT inhibitor, MS023 to dose-dependently increase full length SMN2 splicing SMN protein levels, by decreasing hnRNPA1 binding to SMN2 pre-mRNA. Next, they show that MS023 monotreatment of the severe 'Taiwanese' (+/- SMA type I) mouse model of SMA leads to improved survival and weight gain. Moreover, they show that combinatorial treatment of the same mouse model with MS023 and nusinersen, significantly further improves survival compared to both nusinersen and MS023 monotreatment. Finally, transcriptome analysis suggests that the majority of misregulated transcripts in SMA is rescued by both nusinersen an combinatorial treatment but, importantly, the rescue observed in the combinatorial group seems more complete.

Suggestions

The authors state in the abstract that "transcriptomic analysis revealed that MS023 treatment has very minimal off-target effects". However, their transcriptomic analyses do not contain a condition that investigates the effects of MS023 on the transcriptome in WT and SMA animals on its own. I belief this would have been an essential addition to support the conclusion on off-target effects of MS023, especially considering the benefits that the authors list in the discussion when compared to e.g. VPA. I agree with their comments about the unspecificity of such drugs; however, I don't belief their current transcriptomics analysis on MS023 fully support this conclusion either. It may not be feasible to include such an experiment in a revised version of the manuscript, but in this case the authors should reflect on the wording of their conclusions.

I agree with the authors that the effect of MS023 on SMN-FL RNA appears to be dose-dependent but I don't think the data fully supports that conclusion for SMN protein levels (compare e.g. 250 nM and 2.5 µM quantification). In fact, there are many inconsistencies between SMN RNA and SMN protein levels: in figure 3 (MS023 monotreatment), the authors observe in spinal cord no change in SMN RNA but a significant increase in SMN protein. In contrast, in the same figure, in muscle, both SMN RNA and protein increase significantly. This is a bit confusing and to me mostly means that the regulation of SMN RNA and protein expression in complex and likely depends on many more factors than PMRT activity and hnRNPA1 arginine methylation status. Indeed, the authors pick hnRNPA1 as a promising target from a list of proteins that contains 72 in total. Are there no other promising candidates in this list that would be able to explain the unclear and inconsistent correlation between SMN RNA splicing and SMN protein levels?

The in vitro work was based on the use of one primary fibroblast cell line. It would be relatively straightforward to characterized the effect of MS023 on e.g. type 1 and type 3 patient-derived lines, thus providing a clearer overview of the use of this type of drug in SMA patients of different types. Both through the Corriell repository (as used in the current paper) and surely also through biobanks at Oxford it should be relatively straightforward to obtain such cell lines and for the authors to extend their analyses to include patients of different types (and with varying SMN2 copy number).

The mechanism that the authors suggest in e.g. Fig. 2D about the interaction of hnRNPA1 with the SMN2-ISSN1 in relation to PMRT inhibition is very similar to how nusinersen prevents SMN2-ISSN1 binding of hnRNPA1 (as the authors mention in the discussion). How do the authors suggest this would work? Do they have suggestions for further experiments to investigate this interaction (e.g. using hnRNPA1 and nusinersen molecules with point mutations?)

Minor comments

Do I understand correctly that none of the screened molecules in figure 1 lead to significantly unregulated SMN protein levels (including MS023)? What causes the difference between figure 1 (no signficicant upregulation of SMN protein) vs figure 2 (a dose dependent increase of SMN protein)? Do the authors have an explanation for this difference? In relation to this point, I am somewhat surprised at the variability in protein quantifications in especially figures 1 and 2. In these figures, biological replicates are obtained from one cell line. Although I understand that there is not necessarily much benefit to including all western blots used for quantification in for example the supplementary files with the paper, it would be useful to see some examples for e.g. the western blots for the quantifications in fig. 1C. Similarly, I appreciate the complexity of the IPs and arginine-methylation specific blotting in fig 2E, but the current tightly cropped blots are not super convincing and the uncropped blots are not included in the supplementary data. Also how was this quantified; fig 2F lacks some indication of standard deviation or other indicator of reproducibility between measurements.

There are some what appear to be reference formatting errors (e.g. lines 17 and 20 on page 15 of the manuscript PDF amongst others).

The PDF version of Supplementary table 2 in its current format is not really usable or readable; an Excel version would be preferable.

Significance

The paper addresses an interesting question: it aims to improve the efficacy of existing drugs for SMA by identifying novel molecules that may improve the working mechanism of, in this case, nusinersen. Others have tried this before by using VPA, but the current molecule appears to be more specific. However, it would have been interesting to get more details on the effect of this novel compound: a wider range of cell lines, further mouse experiments (a control group in figs. 3 and 5) and analysis (e.g. pathological analysis of the neuromuscular system). It would in fact have been interesting to combine some of the analyses in the current work also with the other available SMN2 splicing modifier risdiplam: as risdiplam also modulates SMN2 splicing, MS023 might also have been suitable to improve risdiplam efficacy. Especially in the cell line the authors have used this would have been a relatively straightforward addition. I believe the paper may provide an interesting start, but without further analysis remains at that stage.

The audience to likely be most interest are mostly colleagues from the SMA field, as the mechanisms in the current manuscript focus very much on ISS-N1-regulated SMN2 splicing which is highly specific for SMA.

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Reply to the reviewers

Manuscript number: RC-2022-01785

Corresponding author(s): Amélie, Fradet-Turcotte, and Louis, Flamand

Title: The immediate early protein 1 of human herpesvirus 6B counteracts ATM activation in an NBS1-dependent manner

Our manuscript received positive and constructive comments from all three Reviewers. First, they unanimously agreed that the biology uncovered in our study is novel and of broad scientific interest, including researchers studying host-pathogen, DNA damage response and repair processes. They highlighted that the manuscript is well-written and presents clear, rigorous, and convincing data. Second, they provided constructive comments to strengthen our model and the biological relevance of our findings. Here, we provide an overview of our findings and a point-by-point reply explaining the revisions, additional experimentations and analyses planned to address the points raised by the referees.

1 - Description of the planned revisions

1.1 *The three Reviewers agreed that we convincingly show that HHV-6B IE1 binds to NBS1 and inhibits ATM activation; however, they all raised concerns about whether the IE1-dependent inhibition of ATM is required for HHV-6B replication and integration. *

We agree with the Reviewers that the biological data validating the impact of ATM on viral replication and integration could be solidified. Problematically, IE1 is essential to promote HHV-6B replication in infected cells, and thus any IE1 knockdown (KD) or knockout (KO) approach will generate data that are hard to interpret. As mentioned by Reviewers 1 and 3, the ideal experiment to address this concern would be to infect cells with an HHV-6B virus in which IE1 contains a small truncation or a mutation that specifically suppresses its ability to inhibit ATM. Creating IE1 deletion and single mutants in the HHV-6 genome is technically challenging and can only be achieved using herpesvirus bacterial artificial chromosome (BAC)(Warden et al., 2011). Although HHV-6A BAC was previously described (Borenstein & Frenkel, 2009; Tang et al., 2010), our multiple attempts at generating HHV-6B BAC remained unsuccessful. As an alternative, we will investigate if the inhibition of ATM by using the ATM inhibitor (KU-55933) or its depletion by an shRNA, impact HHV-6B replication and integration as proposed by Reviewers 1 and 3. Specifically, MOLT-3 cells will be either treated with 10 µM KU-55933 or depleted for ATM with shATM(Rodier et al., 2009) prior to infection. DMSO and shLUC will be used as controls, respectively. These experiments will allow us to determine if ATM inhibition enhances HHV-6B replication and/or integration.

1.2 Reviewer 2: "Although they have nicely mapped the interaction (between IE1 and NBS1), the authors have not yet defined the mechanism of ATM inhibition. They propose a number of possibilities in the discussion, but none are yet tested experimentally. The manuscript would be strengthened by further exploration of these possibilities. Does the sequence or proposed structure give any insights into interactions that could be relevant? Is IE1 phosphorylated by ATM, and could this affect the binding of other proteins?"

We thank the Reviewer for pinpointing that a deeper characterization of the mechanism of ATM inhibition would allow us to support our model. In the manuscript, we discuss the possibility that IE1 inhibits ATM activation by preventing the interaction between the FxF/Y motif of NBS1 and ATM. Although we do not detect a strong interaction between IE1 and ATM (Fig. 5A), we have not yet investigated if the ATM-inhibitory domain (ATMiD) is required for IE1 to prevent the recruitment of ATM by NBS1 at the LacO array (Fig. 5E). Thus, we will determine if an ∆ATMiD IE1 inhibits the interaction between NBS1 and ATM in this assay. If the ATMiD domain interferes with the interaction of NBS1 with ATM, we expect to see no inhibition of NBS1 activation of ATM in cells that express 3xFlag-HHV-6B IE1 ∆ATMiD.

Another possibility is that IE1 inhibits ATM activation indirectly by interacting with the nucleosome. The latter possibility is based on the finding that the C-terminal domain of HHV-5 IE1 contains an arginine-serine (RS) motif that interacts with the acidic patch of the nucleosome(Fang et al., 2016). Interestingly, HHV-6B IE1 sequence analysis reveals two RS motifs at positions 852-53 and 1033-34. Thus, the conserved RS residues (R852A/S853A and R1033A/S1034A) will be mutated in the ATMiD domain of HHV-6B IE1 (810-1078), and their ability to inhibit ATM activation will be quantified by immunofluorescence approach as described in Fig 6 D-E. In parallel, GST-tagged recombinant ATMiD of HHV-6B IE1 will be produced, and pulldown experiments will investigate their ability to bind to nucleosomes. We already have purified nucleosomes in the lab and have the expertise for this type of analysis(Galloy et al., 2021; Sitz et al., 2019).

Thanks to the Reviewer's comment, we performed sequence analyses for putative ATM phosphorylation sites (SQ/TQ) and found that the protein contains 6 of them, two of which are in the ATMiD of the protein. To determine if the viral protein is a substrate of ATM, we will immunoprecipitate IE1 from MOLT-3 infected cells and use the well-characterized pSQ/pTQ antibody in western blotting analyses. The immunoprecipitation will be done in denaturing conditions to avoid interference with other endogenous interactors of IE1. If the protein is phosphorylated in an ATM-dependent manner, we will test the impact of these mutants on ATM inhibition as done in Fig. 6 D-E.

Altogether, these experiments will allow us to refine our understanding of the mechanism by which HHV-6B IE1 inhibits ATM activation in host cells.

1.3* Reviewer 2: "Could the effects of IE1 be linked to other post-translational modifications? The literature suggests this protein to be SUMOylated. Is SUMOylation relevant to the effects on ATM activation?" *

The Reviewer is right. Our group showed that IE1 is sumoylated on K802R in a SUMO interacting motif (SIM)-dependent manner (V775, I776, V777)(Collin et al., 2020). In the LacO/LacR assays, we already showed that the K802R and SIM mutant (775AAA777) do not impact the interaction of IE1 with NBS1. Although the sumoylated site and the SIM lie outside of the ATMiD, we cannot rule out the possibility that this post-tranlationnal modification impacts ATM inhibition by IE1 throughout a conformational interference. To address this possibility, we will characterize the ability of the single and double K802R/SIM mutant proteins to inhibit the activation of ATM, as described in Fig 6 D-E.

2 - ____Description of the revisions already incorporated in the transferred manuscript

The following comments and all minor comments raised by the Reviewers have been incorporated into the transferred manuscript:

2.1 Reviewer 2: "In Figure 1, they look at micronuclei formation but MNi is not defined the main text."

We thank the Reviewer for noticing this mistake. MNi is now defined as micronuclei in line 138.

2.2 Reviewer 3: "As discussed by the authors, HHV-6B IE1 inhibits DSB signaling through NSB1, but we cannot know how this inhibition (might be increase genome instability of both host and virus) enhances viral replication and integration. The readers are easy to understand if the authors described it in the discussion or analyzed by KD or KO of IE1 in infected cells."

The Reviewer is right. We cannot rule out that increased genomic instability enhances viral replication. Thus, we add the following sentences to clarify this point in the discussion.

Line 371-374: "Finally, the model presented here assumes that NBS1 and ATM activity must be inhibited to prevent their detrimental effect on viral replication. However, it is impossible to rule out that enhanced viral replication and integration result from the increased level of genomic instability induced in host cells upon viral infection. Further studies will be required to address this question."

2.3 Reviewer 3: "Described in lines 354-356 are the case of lytic cycle only. In the lytic cycle, the infected cells will die soon after viral replication. and there is no chance to become tumor. However, the state of ciHHV-6 or latently infected cells can be affected by genome instability during IE1 expression. Please add discussion."

We thank the Reviewer for raising this important point. We agree that the real threat for the host cells regarding tumor development is genomic instability promoted by the expression of IE1 during latent infection or from an integrated form of the virus. Consistent with this possibility, our original manuscript contains this sentence in the abstract:

Line 60-62: "Interestingly, as IE1 expression has been detected in cells of subjects with the inherited chromosomally-integrated form of HHV-6B (iciHHV-6B), a condition associated with several health conditions, our results raise the possibility of a link between genomic instability and the development of iciHHV-6-associated diseases."

To further emphasize this point, the following sentence has now been added to the discussion:

Line 349-356: During the lytic cycle, the accumulation of genomic instability in the host cell genome is not a problem as these cells will die upon the lysis provoked by the virus to release new virus particles. However, more selective inhibition of ATM by IE1 during the latent cycle of HHV-6B or from iciHHV-6B would avoid a detrimental accumulation of genomic alterations in host cells. This model would be consistent with the fact that HHV-6B is not associated with a higher frequency of cancer development, as would be expected if global DSB signaling was inhibited in these cells. Alternatively, expression of IE1 upon the exit of latency may inhibit global DSB signaling, but this phenomenon is restricted to the early stages of the process, thereby minimizing the impact on the host cell's genomic stability.

2.4 Reviewer 3: Line 114, Miura et al (J Infect Dis 223:1717-1723 [2021]) should be cited.

This reference has been added in line 113. In the discussion, we also introduce the citation where we mention the link between HHV-6B integration and abortion, line 362 of the revised manuscript.

3 - ____Description of the revisions that will not be carried out

3.1 Reviewer 2: "Does it (HHV-6B IE1) also share other activities with herpesvirus proteins e.g. ubiquitinylation?"

IE1 shares very little sequence homology with proteins from other herpesviruses (except HHV-6A and HHV-7), meaning that deductions based on primary sequence analysis are very limited. Any attempt at understanding the function of HHV-6B IE1 by structure analysis prediction software did not predict any known function or domain. Thus, most of our knowledge of IE1 relies on experiments that used IE1 truncation (this study and (Jaworska et al., 2007)) and point mutants(Collin et al., 2020). The protein contains no conserved RING or HECT domain that would hint at an E3-ligase activity and does not share homology with other herpes proteins that promote ubiquitylation events, such as ICPO from HSV-1(Rodríguez et al., 2020). We believe that, at this point, there is not enough evidence to investigate further if HHV-6B IE1 has an E3-ligase activity.

3.2 Reviewer 3: Lines 52, "Expression of immediate early protein 1 (IE1) was sufficient to recapitulate this phenotype" is not right. The authors showed that IE1 blocked ATM signaling in transient experiments but they did not show any evidence in infected cells. Kock down or Kock out of IE1 is important to conclude it."

We agree with the Reviewer HHV-6B IE1 knockdown, or knockout, would allow us to conclude that IE1 is the only protein to target DSB signaling in the infected cells. As mentioned by the Reviewer (see point 3.3 and 1.1), IE1 is essential to promote HHV-6B replication in infected cells. Thus, any knockdown or knockout approach will generate data that are hard to interpret. In contrast, the generation of an HHV-6 genome containing truncation or point mutation that abolishes its ability to inhibit ATM signaling should allow us to bypass this issue. While we believe this question is important, human resource shortages prevent us from addressing this point in an acceptable time frame. Instead, we propose investigating the role of ATM activity in HHV-6B replication and integration. We also rephrased the sentence highlighted by Reviewer 3:

Line 51-52: "Expression of immediate early protein 1 (IE1) phenocopies this phenotype and blocks further homology-directed double-strand break (DSB) repair."

3.3 Reviewer 3: The authors did not analyze the effect of viral manipulation as they did not analyze KO or KD of IE1. Even if HHV-6B IE1 is essential for viral replication, they can use dominant negative mutant of IE1 or NSB1 determined in this manuscript.

Reviewer is right. As discussed in points 3.2 and 1.1, we haven’t tried to rescue IE1 knockdown, or knockout in infected cells. Rescue experiments of IE1 by transient transfection of dominant negative IE1 mutant would require a high level of transfection in MOLT-3 cells and small truncation or mutations of IE1 that revert the ATM inhibitory function of IE1. Screening additional sets of truncations/mutants of IE1 that abolish its ability to inhibit ATM and optimizing the poor transfection efficiency of the lymphoid cell line MOLT-3 will take time and resources that we don’t have at this moment. Thus, we believe that this point should be addressed in follow-up studies.

REFERENCES

Borenstein, R., & Frenkel, N. (2009). Cloning human herpes virus 6A genome into bacterial artificial chromosomes and study of DNA replication intermediates. Proceedings of the National Academy of Sciences of the United States of America, 106(45). https://doi.org/10.1073/pnas.0908504106

Collin, V., Gravel, A., Kaufer, B. B., & Flamand, L. (2020). The promyelocytic leukemia protein facilitates human herpesvirus 6B chromosomal integration, immediate-early 1 protein multiSUMOylation and its localization at telomeres. PLoS Pathogens, 16(7). https://doi.org/10.1371/journal.ppat.1008683

Fang, Q., Chen, P., Wang, M., Fang, J., Yang, N., Li, G., & Xu, R.-M. (2016). Human cytomegalovirus IE1 protein alters the higher-order chromatin structure by targeting the acidic patch of the nucleosome. ELife, 5. https://doi.org/10.7554/elife.11911

Galloy, M., Lachance, C., Cheng, X., Distéfano-Gagné, F., Côté, J., & Fradet-Turcotte. (2021). Approaches to study native chromatin-modifying activities and function. Frontiers in Cell and Developmental Biology, Section Epigenomics and Epigenetics, In Press.

Jaworska, J., Gravel, A., Fink, K., Grandvaux, N., & Flamand, L. (2007). Inhibition of Transcription of the Beta Interferon Gene by the Human Herpesvirus 6 Immediate-Early 1 Protein. Journal of Virology, 81(11), 5737–5748. https://doi.org/10.1128/jvi.02443-06

Rodier, F., Coppé, J. P., Patil, C. K., Hoeijmakers, W. A. M., Muñoz, D. P., Raza, S. R., Freund, A., Campeau, E., Davalos, A. R., & Campisi, J. (2009). Persistent DNA damage signalling triggers senescence-associated inflammatory cytokine secretion. Nature Cell Biology, 11(8). https://doi.org/10.1038/ncb1909

Rodríguez, M. C., Dybas, J. M., Hughes, J., Weitzman, M. D., & Boutell, C. (2020). The HSV-1 ubiquitin ligase ICP0: Modifying the cellular proteome to promote infection. In Virus Research (Vol. 285). https://doi.org/10.1016/j.virusres.2020.198015

Sitz, J., Blanchet, S. A. S. A., Gameiro, S. F. S. F., Biquand, E., Morgan, T. M. T. M., Galloy, M., Dessapt, J., Lavoie, E. G. E. G., Blondeau, A., Smith, B. C. B. C., Mymryk, J. S. J. S., Moody, C. A. C. A., & Fradet-Turcotte, A. (2019). Human papillomavirus E7 oncoprotein targets RNF168 to hijack the host DNA damage response. Proceedings of the National Academy of Sciences of the United States of America, 116(39), 19552–19562. https://doi.org/10.1073/pnas.1906102116

Tang, H., Kawabata, A., Yoshida, M., Oyaizu, H., Maeki, T., Yamanishi, K., & Mori, Y. (2010). Human herpesvirus 6 encoded glycoprotein Q1 gene is essential for virus growth. Virology, 407(2). https://doi.org/10.1016/j.virol.2010.08.018

Warden, C., Tang, Q., & Zhu, H. (2011). Herpesvirus BACs: Past, present, and future. In Journal of Biomedicine and Biotechnology (Vol. 2011). https://doi.org/10.1155/2011/124595

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors report that human herpesvirus 6B (HHV-6B) infection suppresses the host cell's ability to induce ATM-dependent signaling pathways. At least one of the viral proteins named IE1 block ATM signaling and further homology-directed double-strand break (DSB) repair in these cells. The ATM-dependent DNA damage response (DDR) is activated by infection of many viruses and suppresses their replications. Some of them induce the degradation of the MRE11/RAD50/NBS1 (MRN) complex and prevent subsequent DDR signaling. In the case of HHV-6B IE1, the N-terminal domain of it interacts with the MRN complex protein NBS1, the interaction of which might recruit IE1 to DSB and the C-terminal domain of IE1 inhibits ATM. The authors also showed that depletion of NBS1 enhanced HHV-6B replication. Viral integration of HHV-6B into the cellular chromosomes was enhanced by the NSB1 depletion in ATL-negative HeLa cells, supporting the models that the viral integration occurs via telomere elongation rather than through DNA repair.

Major comments

This manuscript is well written and will be of interest to the readers. The data seems convincing and statistical analysis is adequate. However, the role and significance of HHV-6B IE1 in infected cells was not analyzed well. If there are not analyzed, the data only show the role of the MRN complex or the only a single protein NSB1 for HHV-6B replication and they cannot conclude that HHV-6B IE1 hampers the ATM signaling for proper viral replication. I have a few comments listed below to improve this manuscript. All of them might be required for a couple of months.

• (i) Lines 52, "Expression of immediate early protein 1 (IE1) was sufficient to recapitulate this phenotype" is not right. The authors showed that IE1 blocked ATM signaling in transient experiment but they did not show any evidence in infected cells. Kock down or Kock out of IE1 is important to conclude it.
• (ii) In Fig7, the role of the other factors in the ATM-dependent DDR (such as ATM) should be analyzed by knock down or inhibitors.
• (iii) The authors did not analyze the effect of viral manipulation as thy did not analyze KO or KD of IE1. Even if HHV-6B IE1 is essential for viral replication, they can use dominant negative mutant of IE1 or NSB1 determined in this manuscript.
• (iv) As discussed by the authors, HHV-6B IE1 inhibit DSB signaling through NSB1, but we cannot know how this inhibition (might be increase genome instability of both host and virus) enhances viral replication and integration. The readers are easy to understand if the authors described it in the discussion or analyzed by KD or KO of IE1 in infected cells.

Minor comments

• (i) Described in lines 354-356 are the case of lytic cycle only. In the lytic cycle, the infected cells will die soon after viral replication. and there is no chance to become tumor. However, the state of ciHHV-6 or latently infected cells can be affected by genome instability during IE1 expression. Please add discussion.
• (ii) Line114, Miura et al (J Infect Dis 223:1717-1723 [2021]) should be cited.

Significance

HHV-6B is ubiquitous herpesvirus which cause exanthem subitem and encephalitis, although effective antiviral is not established yet. Characteristically, HHV-6B has ability to integrate its genome into host. How HHV-6B replicate and integrate its genome in host cells is one of the most important question in this field. I am basic virologist mainly focusing on this virus and believe this manuscript includes important notion for our field.

To counteract ATM-mediated signaling, many viruses induce the degradation of the MRN complex and prevent subsequent DDR signaling. The mechanism of HHV-6B IE1 described in this manuscript is unique and might be interested by the readers from many fields.

Furthermore, around 1% of human populations harbor chromosomally integrated HHV-6B in their genome. The pathogenesis of it is not completely understand but must be important not only for virologist but also all of us.

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Referee #2

Evidence, reproducibility and clarity

Viruses have evolved different strategies by which they manipulate the host DNA damage response (DDR) in order to propagate in infected cells. This study shows how the human herpesvirus 6B (HHV-6B) blocks homology-directed double-stranded DNA break repair by the immediate early protein 1 (IE1) which they demonstrate inhibits the host ATM kinase. They employ microscopy and cytometry approaches to probe genomic instability, signaling, and interactions between virus and host. They use infection of MOLT-3 cells and induction of IE1 in U2OS cells to examine these mechanisms and the effects on genome stability. They show inhibition of H2AX phosphorylation, and inhibition of homology-directed repair with reporter assays. They discovered that IE1 interacts with the cellular NBS1 protein, localizes to DNA breaks, and inhibits activation of ATM kinase. They map two distinct domains that promote NBS1 interaction and the inhibition of ATM activation. They show that depletion of NBS1 promotes lytic replication in MOLT-3 cells, and also decreases the frequency of integration, at least in some semi-permissive cells.

Major:

1. Although they have nicely mapped the interactions, the authors have not yet defined the mechanism of ATM inhibition. They propose a number of possibilities in the Discussion but none are yet tested experimentally. The manuscript would be strengthened by further exploration of these possibilities. Does the sequence or proposed structure give any insights into interactions that could be relevant? Is IE1 phosphorylated by ATM and could this affect binding of other proteins?
2. Could the effects of IE1 be linked to other post-translational modifications? The literature suggests this protein to be SUMOylated. Is SUMOylation relevant to the effects on ATM activation? Does it also share other activities with herpesvirus proteins e.g. ubiquitinylation?
3. Are the effects on the lifecycle (lytic replication and integration) affected by ATM kinase in the same way as NBS1?

Minor:

1. In Figure 1 they look at micronuclei formation but MNi is not defined the main text.

Significance

Overall, the manuscript is well written the experiments are performed in a rigorous manner, and the biology uncovered is of broad scientific interest. It is now known that a number of DNA viruses inhibit aspects of the cellular DNA sensing and repair machinery to overcome antiviral responses and promote infection. Understanding how this achieved by different viral systems provides insights into cellular DNA damage signaling and repair. It also informs about how viruses can trigger genomic instability. In this case, the authors have uncovered a novel way that the ATM kinase is inhibited during HHV-6B infection by the IE1 protein. They show that HHV-6B infection induces genomic instability. Integration of the HHV-6 genome results in inherited chromosomally-integrated (ici)HHV-6A/B. They have some data to show that virus replication is inhibited by NBS1 and that viral integration may be partially impacted. These results have implications for understanding viral integration and genomic instability with this human pathogen. They advance the field and expand our understanding of how viruses manipulate repair pathways and lead to genomic instability. Strengths include the rigorous analysis of interactions with IE1 and impacts on cellular pathways. Limitations include the lack of mechanism for inhibition and the weaker links to viral biology. The results will be on interest to those studying virus-host interactions as well as those studying repair pathways beyond virus infection.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript Collin and colleagues found that the human herpesvirus 6B (HHV-6B) causes genomic instability in host cells by suppressing the host cell's ability to induce ATM-dependent signaling pathways. The authors show that the immediate early protein 1 (IE1) of HHV-6B is sufficient to block homology-directed double-strand break (DSB) repair and ATM-mediated DNA damage signaling. Interestingly, the authors show that IE1 does not affect the stability of the MRN complex, but instead uses two distinct domains to inhibit ATM activation. Finally, the authors show that suppression of NBS1 is critical for the ability of HHV-6B to replicate in permissive cells. In contrast, suppression of NBS1 increases the rate of integration in semi permissive cells. Overall, this study provides a mechanistic insight into HHV-6B infection and viral integration into telomeres may promote genomic instability and the development of certain diseases associated with inherited chromosomally integrated form of HHV-6B.

Significance

Overall, this is a superb manuscript, the data are clear, well controlled, and well presented. This reviewer has only a minor suggestion/ comment.

The authors show convincingly that E1a can bind NBS1 and suppress ATM activation. However, it is not clear whether suppression of ATM is critical for HHV-6 replication. The ideal experiment would be an infection with a virus depleted of E1A (or expressing a defective E1A mutant). I realize that this would be a challenging experiment. An alternative experiment would be to test whether suppression of ATM has the same effect on HHV-6 replication and integration as NBS1 depletion.

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Reply to the reviewers

Manuscript number: RC-2022-01803

Corresponding author(s): Brittany A., Ahlstedt, Rakesh, Ganji, Sirisha Mukkavalli, Joao A., Paulo, Steve P., Gygi, Malavika, Raman

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1. General Statements [optional]

This section is optional. Insert here any general statements you wish to make about the goal of the study or about the reviews.

We thank the reviewers for their insightful comments and agree that the many of these revision experiments will improve the strength of our manuscript. Some of these we have already completed or are in the process of completing which will be outlined below. In particular, the reviewers asked that we investigate the mechanistic link between increased translation and UPR induction. We have detailed the studies that we will perform to establish this connection in detail below.

Description of the planned revisions

Response to Reviewer 1:

1. The authors need to express UBXN1 and mutants lacking either the UBX or UBA domain in UBXN1 knockout cells to test whether the ER stress phenotype (Figure 1) and the protein upregulation phenotype (Figure 5A-F) can be rescued. This would eliminate the possibility that the reported phenotypes are the off-target effects of CRISPR.
2. We will express the Myc-tagged wildtype UBXN1 and UBX or UBA point mutants (used in translation rescue studies in Figure 6) into UBXN1 knockout (KO) cells to determine whether the ER stress phenotype can be rescued. We will determine the level of xbp1s by real-time PCR and BiP by immunoblot.
3. The studies in Figure 5 A-F were completed in cells depleted of UBXN1 with siRNA, not the CRISPR knockout cells. Thus, it is unlikely an off-target effect of CRISPR. We will attempt rescue of this phenotype with the wildtype and mutant constructs.

For Figure 2, please indicate whether the repeat is a biological replicate or a technical replicate from RT-PCR.

• We apologize for the omission. The data from the RT PCR studies in Figure 2 are biological replicates – the figure legend and main text of the manuscript will be edited to clarify this.

In Figure 1A, the authors show that the knockout of UBXN1 causes an upregulation of phosphorylated eIF2alpha, which is known to suppress protein translation globally. In this regard, it is surprising to see the authors also concluded from Figure 7 that there is an upregulation of protein translation in UBXN1 knockout cells. The authors do not provide any explanation on how these seemingly contradictory phenotypes could be seen in the same cells.

• We will provide a detailed discussion of the apparent paradox between upregulation of phosphorylated eIF2a and increased protein translation. Several prior studies have demonstrated that elevated expression of ATF4 (as we observe in UBXN1 KO cells) activates a transcriptional program that restarts translation. This occurs through the upregulation of the phosphatase PPP1R15a that dephosphorylates eiF2a, as well as aminoacyl tRNA synthetases and ribosomal subunits. We propose that elevated ATF4 levels leads to premature translational restart in UBXN1 KO cells. In addition, our data suggests that UBXN1 represses translation upstream of UPR activation and thus and increase in protein translation dysregulates ER-proteostasis which hyperactivates the UPR.

Any evidence that UBXN1 is associated with translating ribosomes?

• We now have new data that UBXN1 is associated with 40S, 60S, and 80S ribosomal fractions as well as actively translating polysome fractions that we isolated by polysome purification. In agreement with our finding that the role of UBXN1 in repressing translation is independent of p97, p97 appears to associate largely with the 40S, 60S, and 80S ribosomal fractions but not with the actively translating polysomes. This data will be included in the revised manuscript. Response to Reviewer 2:

• Authors found that significant enrichment of the ER proteins in UBXN1 KO cells, while there is no change in the abundance of proteins in the cytosol or nucleus. Mitochondrial proteins are even down-regulated in UBXN1 KO cells. I found these observations very interesting. However, I was frustrated that authors did not investigated the reason why such differences are associated in UBXN1-suppressed cells. Authors demonstrate that depletion of UBXN1 resulted in suppression of protein synthesis, but did not address whether ER proteins are specifically repressed by UBXN1 or it represses translation globally, as noted in their Discussion section. Do the mRNAs encoding signal sequence at the N-terminus of their products are specifically translated in UBXN1-suppressed cells? Do the translations of mRNAs encoding mitochondria translocation signals are suppressed in UBXN1 KO cells? It should be possible to investigate these issues by using appropriate model ER- or mitochondrial proteins with or without specific signal sequences. Such kind of analysis should be necessary to support the claim of this manuscript.

• Previous studies by Luke Wiseman’s group showed that PERK activation resulted in hyperfusion of the mitochondria and loss of Tim17 leading to decreased mitochondrial import. We already show that mitochondrial proteins are downregulated (by TMT proteomics and by immunoblotting). We now have preliminary data that mitochondria are more fused in UBXN1 KO cells consistent with data from the Wiseman group. We will include this in the resubmission.
• In addition, we have re-analyzed our TMT proteomics data to parse out proteins with ER-signal sequences and define the topology of ER proteins (Type 1, 2, multimembrane spanning and luminal proteins) and those with mitochondrial targeting sequences. This data will be included in the revised manuscript.

Related to my previous comments, ER-targeted mRNAs are known to be degraded by a process termed RIDD in the case of ER stressed condition. Since the rapid degradation of mRNAs through RIDD functions to alleviate ER stress by preventing the continued influx of new polypeptides into the ER, I wondered why UBXN1 depletion greatly stimulates ER protein synthesis, escaping IRE1-dependent mRNA degradations. Does UBXN1 depletion suppress RIDD?

• In the revised manuscript, we will determine the relative mRNA abundance of the bona fide RIDD targets BLOC1S1 and CD59 by quantitative PCR in cells stressed with dithiothreitol (DTT). We will utilize previously published and validated primers for each target to quantify RIDD activity in wildtype and UBXN1 KO cells. These studies will address whether loss of UBXN1 impacts IRE1-dependent RIDD.

Authors mentioned that the elevated levels of ER proteins are not due to increased transcription of target genes. However, they only provided the quantification of prp transcript levels, which was unchanged between wildtype and UBXN1 KO cells. To support this important conclusion, it is necessary to provide whole transcriptome data to compare the expression levels of corresponding ER proteins (quantified by their proteomics data) and transcripts (quantified by, for an example, RNA-seq analysis).

• We thank the reviewer for this comment. Currently, we show that mRNA levels of Prp do not significantly change between control and siUBXN1 cells (Supplementary Figure 4). For a more comprehensive analysis, we will additionally assess the mRNA levels of the proteins we determinized to be significantly enriched in Figure 5 (AGAL, ALPP2 and TRAPa). RNA sequencing is currently beyond the scope of this study.

Authors claimed that UBXN1 loss is detrimental to cell viability and have elevated levels of the apoptosis in the face of ER stress. However, authors did not examine apoptotic cell death in UBXN1 KO cells. They only provided evidence for defective proliferation of cells and transient induction of CHOP expression, but these are not enough to support the ER-stress induced apoptosis.

• We will address the levels of apoptotic cell death in wildtype and UBXN1 KO cells by assessing PARP, caspase-3, or caspase-8 cleavage in these cells by immunoblot.

Authors showed that UBA domain of UBXN1 is critical for suppressing protein synthesis. Could you provide a bit more detailed discussion how UBA domain modulates protein translational events and promote expressions of ER-related proteins. Have you ever checked whether UBA domain of UBXN1 is necessary for suppressing UPR-specific target gene expressions?

• We will express the Myc-tagged wildtype UBXN1 and UBX or UBA point mutants (used in translation rescue studies in Figure 6) into UBXN1 knockout (KO) cells to determine whether the ER stress phenotype can be rescued.
• We will also include a discussion on how the UBA domain in UBXN1 may recognize distinct ubiquitylation events on ribosomes that modulate their abundance and function. Response to Reviewer 3:

(Major comments)

1. My main reservation about the current manuscript is whether the UPR activation can be directly ascribed to the loss of UBXN1. The authors do not differentiate between acute depletion (through siRNA in Fig. 5) versus permanent UBXN1 knockout in most of the experiments. The latter may lead to extensive adaptation of the cellular proteome due to chronic stress. Prior studies from the authors have shown that UBXN1 knockout leads to loss of aggreasomes. This raises a major question whether the observed UPR activation can be directly attributed to UBXN1 loss or be an indirect result of adaptation in the knockout cells, for instance due to accumulation of BAG6 substrates in insoluble aggregates as the authors have shown previously (ref. 40). Along those lines, the authors already showed in the same study that UBXN1 knockout cells are more sensitive to proteotoxic stress.
2. We agree with the reviewer that cells can adapt to CRISPR knockout. However, the IRE1a clustering studies found in Figure 1 were completed in the context of acute depletion of UBXN1 by siRNA and demonstrate a significant increase in IRE1a clustering when UBXN1 is depleted.
3. We now have new data that that acute depletion of UBXN1 with siRNA results in a significant increase in BiP and ATF4 expression as well as ATF6 N-terminal processing.
4. Furthermore, we have new data that acute depletion of UBXN1 with siRNA phenocopies UBXN1 KO in terms of increased puromycin incorporation into newly synthesized proteins.
5. Thus, we will have both genetic knockout as well as siRNA acute depletion for all major studies. We will include these new studies in the revised manuscript.

The later results in the study nicely show that the repressed protein translation phenotype is dependent on the ubiquitin binding domain of UBXN1. These segregation-of-function mutants and complementation experiments could be easily used to more clearly distinguish whether the UPR activation can be directly attributed to UBXN1 and the increase in protein translation. For instance, can overexpression of UBXN1 in the knockout background suppress the UPR activation? Is the UBX-domain mutant capable of suppressing the UPR phenotype? These results would provide critical support as to whether the UPR activation is a direct result of the loss of UBXN1.

• We will express the Myc-tagged wildtype UBXN1 and UBX or UBA point mutants (used in translation rescue studies in Figure 6) into UBXN1 knockout (KO) cells to determine whether the ER stress phenotype can be rescued. We will determine the level of xbp1s by real-time PCR and BiP by immunoblot.
• To delineate the relationship between UPR activation and protein translation, we will halt protein synthesis with the translational elongation inhibitor cycloheximide and assess UPR activation in wildtype and UBXN1 KO cells. If increased protein translation in UBXN1 KO cells is what causes UPR activation, we anticipate that cycloheximide will rescue UPR activation in UBXN1 KO cells back to wildtype levels.

Similarly, the authors use transient siRNA knockdown of UBXN1 in Fig. 5 and Supp. Fig. 4, but do not reassess the UPR activation under these conditions. It would be important to validate that the acute UBXN1 knockdown can recapitulate the UPR activation phenotype.

• Please see comment 1 above.

I am puzzled by the interpretation of the AGAL degradation experiments in Supplemental Figure 4F. Clearly, the rate of AGAL degradation is much faster in WT cells than in UBXN1 knockout cells as indicated by the slope of the curves between 2-4 hours. I disagree with the interpretation that UBXN1 knockout does not impact AGAL turnover. It is not valid to make the comparison at 9 hours because hardly any AGAL substrate is remaining. Importantly, this experiment raises a larger question: Are other ER client degradation rates affected by the UBXN1 knockout? And is the UPR activation more generally due to accumulation of misfolded ER proteins? Their prior publication (ref. 40) evaluated several ERAD clients where UBXN1 was dispensable, but it could be possible that UBXN1 has a more specialized client pool. Showing quantification of the PrP CHX chase would also be helpful - from the single replicate it looks like more PrP remaining in the UBXN1 knockout at 8 hours (Supp. Figure 4G).

• Our previous ERAD reporter study using three distinct ERAD clients that are routinely used to assess ERAD found no role for UBXN1 in ERAD (Ganji et al MCB 2018). We do agree with the reviewer that UBXN1 may have discrete roles in regulating the degradation of select p97 ER clients. Determining this in an unbiased and comprehensive manner would require pulse chase SILAC proteomics or similar methodologies which are beyond the scope of the current study. We will therefore evaluate whether loss of UBXN1 affects the rate of degradation of additional ER-client proteins that we identified via TMT. Additionally, we will include a quantification of PrP cycloheximide chase.

It would be helpful for the manuscript to clearly distinguish between 1) upregulation of ER proteostasis factors because of ER stress/UPR, and 2) upregulation of secreted clients (AGAL, PrP) which may be partly due to increased translation rates but could also be due to reduced degradation. Many of the hits from the proteomics experiments are ER proteostasis factors that are part of the adaptive stress response (SEC61B, SEC63, CANX, SSR1/2/3, STT3B, RPN1, RPN2, SEC61A1 - compare to ref 12: most are direct IRE1/XBP1s targets). Their increased expression does not lead to increased ER stress as they are involved in the resolution of ER stress. It appears to be circular logic that increased expression of UPR targets would lead to more UPR activation. Currently, the authors do not clearly disentangle the increased expression of endogenous ER proteins from the proteomics experiment versus overexpression of exogenous secreted clients.

• We identify many ER proteins with increased abundance in UBXN1 KO cells that are not transcriptional targets of the IRE1-UPR pathway. We will re-format the TMT data to more comprehensively characterize the proteins that we identify (known UPR transcriptional targets, membrane embedded, soluble clients etc.).
• We will change the language in the current manuscript to clearly demarcate the difference between an increase of ER proteostasis factors in response to ER stress, and the upregulation of secreted proteins. Additionally, we will emphasize the secretory proteins that are significantly enriched in UBXN1 KO cells in our proteomics figures to demonstrate the increase of non-ER stress responsive clients.

The authors should tone down on broad generalizations, for instance in lines 306-309: ER aggregation was only observed for a single client protein (AGAL). Further, only a single mitochondrial protein was observed to be downregulated (TOMM20).

• We have included the quantifications of the relative expression levels of three mitochondrial proteins, two of which are significantly reduced (TOMM20 and CYC1).
• Additionally, we have new data where we immunoblotted for additional mitochondrial import factors and observed significant reduction of the mitochondrial proteins TIMM23 and TOMM70A which will be included in the revised manuscript.
• We also plan to examine the levels of the TIMM17A subunit of the TIMM23 complex in UBXN1-depleted cells. TIMM17A is degraded in response to ER stress to prevent protein import into the mitochondria. (Rainbolt, T. et al. Cell Metab 2013)
• The language of the manuscript will be changed to tone down on broad generalizations. (Minor comments)

Does UBXN1 localization to the ER/microsomes fraction depend on p97? What happens in UBX-domain mutant?

• We will isolate ER-microsomes from UBXN1 KO cells where we have expressed wildtype and UBX/UBA domain mutants to address if localization is dependent on ubiquitin or p97 interaction.

In Fig. 1A it is surprising that no BiP is detected at 0 hours as BiP is highly expressed even in the absence of ER stress. Can the authors comment on this discrepancy.

• We provide low exposures of the immunoblots as the UBXN1 KO cells have very high levels of BiP compared to control. We will provide alternative blots where the BiP levels at t=0 in control cells is more obvious.

The authors use different ER stressors interchangeably: DTT, Tunicamycin, Thapsigargin. While all results in UPR activation, they do so through different mechanisms and with slight nuances that may be worth considering for the experiments and interpretations.

• We thank the reviewer for this comment and agree that these stressors can impact the ER and UPR activation in distinct ways. Our rationale for using these agents interchangeably was to demonstrate the UPR induction in UBXN1 null cells occurs irrespective of the type of stress.
• DTT is a severe stressor and we used tunicamycin and thapsigargin in some assays (imaging etc.) as they are less toxic and more amenable to downstream analysis. We will include text that explains our rationale better.

Line 198: "Hierarchical clustering analysis demonstrates that the gene expression pattern observed in UBXN1 KO cells more closely resembles wildtype cells stressed with DTT than untreated wildtype cells based on similar log2 fold change values (Figure 2)." Where is this clustering shown?

• We apologize that this was not clear in the figure. We will edit the figure to make the clustering more obvious.

What are the downregulated UPR genes in Fig. 2, and may this hold significance?

• The reviewer points out an interesting observation. Many of the downregulated transcripts are ERAD components. The significance of this is presently unclear and we would require RNA-seq analysis to make a more educated conclusion. However, this finding may point to an environment that has a greater need to induce folding than degradative components. We will include a discussion of this in the revision.

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

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

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

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

Response to Reviewer 1:

1. Taking the increased protein translation phenotype as an example, does this indicate UBXN1 is a translation suppressor for those ER-associated proteins?
2. We thank the reviewer for this comment. We are indeed very interested in determining whether UBXN1 represses the translation of ER proteins. We are in the process of identifying proteins that are translated in UBXN1 null cells using O-propargyl-puromycin (OPP) labelling and mass spectrometry. However, given the timeframe for these studies, this cannot be accomplished in this revision.

How can UBXN1 selectively inhibit the translation of a subset of proteins?

• Recent studies suggest that ribosome populations are quite heterogeneous, and ribosome associated proteins can help tune translation of select proteins. For example, pyruvate kinase muscle (PKM) associates with ER docked ribosomes to regulate the translation of ER proteins in particular. We find that UBXN1 is present on ER membranes and localizes to polysomes and thus may regulate the translation of specific proteins. Studies are underway to test this hypothesis but are beyond the scope for this present study. Response to Reviewer 2:

• Authors found that significant enrichment of the ER proteins in UBXN1 KO cells, while there is no change in the abundance of proteins in the cytosol or nucleus. Mitochondrial proteins are even down-regulated in UBXN1 KO cells. I found these observations very interesting. However, I was frustrated that authors did not investigated the reason why such differences are associated in UBXN1-suppressed cells. Authors demonstrate that depletion of UBXN1 resulted in suppression of protein synthesis, but did not address whether ER proteins are specifically repressed by UBXN1 or it represses translation globally, as noted in their Discussion section. Do the mRNAs encoding signal sequence at the N-terminus of their products are specifically translated in UBXN1-suppressed cells? Do the translations of mRNAs encoding mitochondria translocation signals are suppressed in UBXN1 KO cells? It should be possible to investigate these issues by using appropriate model ER- or mitochondrial proteins with or without specific signal sequences. Such kind of analysis should be necessary to support the claim of this manuscript.

• Please see comment 1 above.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Ahlstedt et al. investigate a new role for the p97 adapter protein UBXN1 in negatively regulating the ER unfolded protein response. The study starts from the observations that knockdown of UBXN1 in a previously generated HeLa cell line leads to induction of unfolded protein response markers, and the knockout cells display more pronounced UPR activation upon ER stress. This elevated UPR signaling renders the UBXN1 cells more prone to cell death. Global proteomics experiments similarly show an increased abundance of ER localized proteins, although it is not clearly delineated which of those are the result of UPR activation. The authors then probe the expression of two secretory client proteins, alpha-galactosidase (AGAL) and prion protein (PrP) and find that UBXN1 transient knockdown leads to ER accumulation of the two proteins and increased aggregation upon ER stress. The authors claim that degradation of these ER client proteins in unaffected by the UBXN1 knockdown, but accumulation may instead be due to increased protein translation. Indeed, they surprisingly find that UBXN1 knockout leads to constitutively elevated protein translation. This result points to a previously unknown role of UBXN1 in repressing protein synthesis. Complementation with UBXN1 mutants demonstrate that the translation repression is dependent on the ubiquitin binding activity of UBXN1 but that p97 is dispensable. Further investigation into the molecular mechanism for the translation repression remains reserved for a future manuscript.

Major comments:

1. My main reservation about the current manuscript is whether the UPR activation can be directly ascribed to the loss of UBXN1. The authors do not differentiate between acute depletion (through siRNA in Fig. 5) versus permanent UBXN1 knockout in most of the experiments. The latter may lead to extensive adaptation of the cellular proteome due to chronic stress. Prior studies from the authors have shown that UBXN1 knockout leads to loss of aggreasomes. This raises a major question whether the observed UPR activation can be directly attributed to UBXN1 loss or be an indirect result of adaptation in the knockout cells, for instance due to accumulation of BAG6 substrates in insoluble aggregates as the authors have shown previously (ref. 40). Along those lines, the authors already showed in the same study that UBXN1 knockout cells are more sensitive to proteotoxic stress.
2. The later results in the study nicely show that the repressed protein translation phenotype is dependent on the ubiquitin binding domain of UBXN1. These segregation-of-function mutants and complementation experiments could be easily used to more clearly distinguish whether the UPR activation can be directly attributed to UBXN1 and the increase in protein translation. For instance, can overexpression of UBXN1 in the knockout background suppress the UPR activation? Is the UBX-domain mutant capable of suppressing the UPR phenotype? These results would provide critical support as to whether the UPR activation is a direct result of the loss of UBXN1.
3. Similarly, the authors use transient siRNA knockdown of UBXN1 in Fig. 5 and Supp. Fig. 4, but do not reassess the UPR activation under these conditions. It would be important to validate that the acute UBXN1 knockdown can recapitulate the UPR activation phenotype.
4. I am puzzled by the interpretation of the AGAL degradation experiments in Supplemental Figure 4F. Clearly, the rate of AGAL degradation is much faster in WT cells than in UBXN1 knockout cells as indicated by the slope of the curves between 2-4 hours. I disagree with the interpretation that UBXN1 knockout does not impact AGAL turnover. It is not valid to make the comparison at 9 hours because hardly any AGAL substrate is remaining. Importantly, this experiment raises a larger question: Are other ER client degradation rates affected by the UBXN1 knockout? And is the UPR activation more generally due to accumulation of misfolded ER proteins? Their prior publication (ref. 40) evaluated several ERAD clients where UBXN1 was dispensable, but it could be possible that UBXN1 has a more specialized client pool. Showing quantification of the PrP CHX chase would also be helpful - from the single replicate it looks like more PrP remaining in the UBXN1 knockout at 8 hours (Supp. Figure 4G).
5. It would be helpful for the manuscript to clearly distinguish between 1) upregulation of ER proteostasis factors because of ER stress/UPR, and 2) upregulation of secreted clients (AGAL, PrP) which may be partly due to increased translation rates but could also be due to reduced degradation. Many of the hits from the proteomics experiments are ER proteostasis factors that are part of the adaptive stress response (SEC61B, SEC63, CANX, SSR1/2/3, STT3B, RPN1, RPN2, SEC61A1 - compare to ref 12: most are direct IRE1/XBP1s targets). Their increased expression does not lead to increased ER stress as they are involved in the resolution of ER stress. It appears to be circular logic that increased expression of UPR targets would lead to more UPR activation. Currently, the authors do not clearly disentangle the increased expression of endogenous ER proteins from the proteomics experiment versus overexpression of exogenous secreted clients.
6. The authors should tone down on broad generalizations, for instance in lines 306-309: ER aggregation was only observed for a single client protein (AGAL). Further, only a single mitochondrial protein was observed to be downregulated (TOMM20).

Minor comments

• Does UBXN1 localization to the ER/microsomes fraction depend on p97? What happens in UBX-domain mutant?
• In Fig. 1A it is surprising that no BiP is detected at 0 hours as BiP is highly expressed even in the absence of ER stress. Can the authors comment on this discrepancy.
• The authors use different ER stressors interchangeably: DTT, Tunicamycin, Thapsigargin. While all results in UPR activation, they do so through different mechanisms and with slight nuances that may be worth considering for the experiments and interpretations.
• Line 198: "Hierarchical clustering analysis demonstrates that the gene expression pattern observed in UBXN1 KO cells more closely resembles wildtype cells stressed with DTT than untreated wildtype cells based on similar log2 fold change values (Figure 2)." Where is this clustering shown?
• What are the downregulated UPR genes in Fig. 2, and may this hold significance?

Significance

General assessment: The authors broadly characterize the UPR activation in the UBXN1 knockout cells, looking both at gene targets by Western blot and qPCR, and characterize the activation of individual sensors (ATF6 cleavage and IRE1alpha clustering). Proteomics results further corroborate the upregulation of ER-localized proteins, although the robustness of the findings is surprising considering that only 2 replicates were included in the mass spectrometry experiment. Most other experiments are technically sound, for instance the puromycilation translation assays. One of the key limitations of the is that the authors fail to make use of their extensive prior toolset on UBXN1, particularly the segregation-of-function mutations for p97 and ubiquitin binding, as well as the knockdown cell lines with inducible overexpression of UBXN1 to rescue the phenotypes. These tools could probe a direct involvement of UBXN1 in the UPR repression, and whether this activity is truly independent of p97. A related limitation is that results are often over-interpreted and too far generalized (see examples above), or wrongly interpreted (see AGAL degradation rates).

Advance: The AAA+ ATPase VCP/p97 has many divergent cellular roles that are in part mediated by a variety of different adaptor proteins. The authors have previously discovered the important role for UBXN1 in recruiting p97 to mislocalized cytosolic proteins targeted to the BAG6 complex. The current study now aims to establish a new role for UBXN1 in regulating the unfolded protein response. As it stands, the findings that UBXN1 knockdown results in UPR activation and impacts translation rates are solid but largely descriptive in nature. These findings merit reporting but require that the authors tone down their conclusions about a direct role for UBXN1 as a regulator of the UPR. Alternatively, if the authors choose to stick with their current model for a direct involvement of UBXN1, they need to establish the mechanistic link more clearly.

Audience: In the current form, the manuscript should appeal to a broad biochemistry and cell biology readership interested in topics related to proteostasis, protein quality control, and stress signaling.

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Referee #2

Evidence, reproducibility and clarity

RC-2022-01803 "UBXN1 maintains ER proteostasis and represses UPR activation by modulating translation independently of the p97 ATPase" By Ahlstedt et al.

Comments to the Author

UBXN1 is a VCP adaptor UBX domain protein which is known to be involved in elimination of ubiquitylated cytosolic proteins bound to the BAG6 complex. In this study, authors demonstrated that cells depleted of UBXN1 have elevated UPR activation, even without external ER stresses. Cells devoid of UBXN1 have significant and global up-regulation of UPR-specific target genes, and these cells are more sensitive to ER stress than their wildtype counterparts. Using quantitative tandem mass tag proteomics of UBXN1 deleted cells, authors found that significant enrichment of the abundance of ER proteins involved in protein translocation, protein folding, quality control, and the ER stress response in an ERAD-independent manner. Notably, they observed no change in the abundance of proteins in the cytosol or nucleus, and significant decrease in the expression of several mitochondrial proteins when UBXN1 was depleted. Authors further demonstrate that UBXN1 is a translation repressor, and its UBA domain is critical for suppressing protein synthesis. Thus, increased influx of proteins into the ER in UBXN1 KO cells causes UPR activation. Authors concluded that they have identified a new regulator of protein translation and ER proteostasis.

My specific comments were provided as follows.

Comments

1. Authors found that significant enrichment of the ER proteins in UBXN1 KO cells, while there is no change in the abundance of proteins in the cytosol or nucleus. Mitochondrial proteins are even down-regulated in UBXN1 KO cells. I found these observations very interesting. However, I was frustrated that authors did not investigated the reason why such differences are associated in UBXN1-suppressed cells. Authors demonstrate that depletion of UBXN1 resulted in suppression of protein synthesis, but did not address whether ER proteins are specifically repressed by UBXN1 or it represses translation globally, as noted in their Discussion section. Do the mRNAs encoding signal sequence at the N-terminus of their products are specifically translated in UBXN1-suppressed cells? Do the translations of mRNAs encoding mitochondria translocation signals are suppressed in UBXN1 KO cells? It should be possible to investigate these issues by using appropriate model ER- or mitochondrial proteins with or without specific signal sequences. Such kind of analysis should be necessary to support the claim of this manuscript.
2. Related to my previous comments, ER-targeted mRNAs are known to be degraded by a process termed RIDD in the case of ER stressed condition. Since the rapid degradation of mRNAs through RIDD functions to alleviate ER stress by preventing the continued influx of new polypeptides into the ER, I wondered why UBXN1 depletion greatly stimulates ER protein synthesis, escaping IRE1-dependent mRNA degradations. Does UBXN1 depletion suppress RIDD?
3. Authors mentioned that the elevated levels of ER proteins are not due to increased transcription of target genes. However, they only provided the quantification of prp transcript levels, which was unchanged between wildtype and UBXN1 KO cells. To support this important conclusion, it is necessary to provide whole transcriptome data to compare the expression levels of corresponding ER proteins (quantified by their proteomics data) and transcripts (quantified by, for an example, RNA-seq analysis).
4. Authors claimed that UBXN1 loss is detrimental to cell viability and have elevated levels of the apoptosis in the face of ER stress. However, authors did not examine apoptotic cell death in UBXN1 KO cells. They only provided evidence for defective proliferation of cells and transient induction of CHOP expression, but these are not enough to support the ER-stress induced apoptosis.
5. Authors showed that UBA domain of UBXN1 is critical for suppressing protein synthesis. Could you provide a bit more detailed discussion how UBA domain modulates protein translational events and promote expressions of ER-related proteins. Have you ever checked whether UBA domain of UBXN1 is necessary for suppressing UPR-specific target gene expressions?

Significance

Although the discovery in this manuscript might be potentially interesting for broad audience, the presented study did not provide enough mechanistic insights and their data lacks vital evidences to support their conclusion. I found that the data are preliminary to discuss the validity of this finding. The inadequacy of these points makes this manuscript unsuitable for publication at this stage.

My expertise is cell biology and biochemistry for protein quality control.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Ahlstedt et al. study UBXN1, an adaptor of the p97/VCP AAA ATPase, using a cell line deficient for UBXN1. They found that the knockout of UBXN1 activates ER stress and sensitizes cells to ER stress-induced cell death. They used a proteomic approach to analyze the change in the global proteome in UBXN1 knockout cells. Interestingly, they found many proteins are upregulated in UBXN1 knockout cells, which appears to be regulated at a post-transcriptional level. Using puromycin labeling, they found that protein translation appears to be upregulated in UBXN1 knockout cells.

Major comments:

The conclusions of the manuscript are generally well supported by experimental data, which are of high quality. The presentation is clear. In my opinion, a few issues need to be addressed to further strengthen their conclusions. 1. The authors need to express UBXN1 and mutants lacking either the UBX or UBA domain in UBXN1 knockout cells to test whether the ER stress phenotype (Figure 1) and the protein upregulation phenotype (Figure 5A-F) can be rescued. This would eliminate the possibility that the reported phenotypes are the off-target effects of CRISPR. 2. For Figure 2, please indicate whether the repeat is a biological replicate or a technical replicate from RT-PCR. 3. In Figure 1A, the authors show that the knockout of UBXN1 causes an upregulation of phosphorylated eIF2alpha, which is known to suppress protein translation globally. In this regard, it is surprising to see the authors also concluded from Figure 7 that there is an upregulation of protein translation in UBXN1 knockout cells. The authors do not provide any explanation on how these seemingly contradictory phenotypes could be seen in the same cells.

Significance

p97/VCP is an important member of the AAA ATPase family that has a variety of functions. It interacts with a collection of adaptor proteins that all contain a UBX domain. These adaptors help to link the ATPase to the correct substrate in cells. The best-established function of p97/VCP is its role in ERAD, in which it acts together with its adaptors Ufd1-Npl4 and UBXD8 to extract retrotranslocated proteins from the ER for proteasomal degradation. UBXN1 is not required for ERAD. Instead, it appears to be a negative regulator of ERAD. Previous studies have also implicated it in mitophagy (Mengus C., Autophagy, 2022) and aggresome formation (from this group). Overall, the published studies did not pinpoint the precise cellular function of UBXN1.

This work characterizes the cellular phenotypes associated with UBXN1 loss of function. The information reported here is important, but the biological significance is limited. This is mainly because the authors entirely rely on a genetic approach. While the reported phenotypes associated with UBXN1 deficiency is solid, it is unclear what the underlying mechanisms are. It is not clear whether or not these phenotypes are interconnected, nor is it clear whether UBXN1 is a direct regulator of these processes. Taking the increased protein translation phenotype as an example, does this indicate UBXN1 is a translation suppressor for those ER-associated proteins? How can UBXN1 selectively inhibit the translation of a subset of proteins? Any evidence that UBXN1 is associated with translating ribosomes?

In summary, because of the limited mechanistic insights on UBXN1 function, the study may only be interesting to a specialized audience.

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Reply to the reviewers

• Reviewer #1 (Evidence, reproducibility and clarity (Required))*

Summary: ER+ breast cancer is the most common form of cancer. Targeting ER-alpha transcriptional cofactors present one potential method to target the disease. The authors demonstrate that MYSM1 is a histone deubiquitinase and a novel ER cofactor, functioning by up-regulating ER action via histone deubiquitination. Loss of MYSM1 attenuated cell growth and increase breast cancer cell lines' sensitivity to anti-estrogens. The authors, therefore, propose MYSM1 as a potential therapeutic target for endocrine resistance in Breast cancer. *

*Major Comments: *

The data as presented is convincing, and the evidence for the role of MYSM1 as a co-activator of ER-alpha is extensive. Given the amount of data, I do not believe any additional experiments are needed. I could not find any description of ethics for the patient samples used.

Response: Appreciate for the positive response from the reviewer. According to the important suggestions, the ethics approval for the patient specimens have been included in the “Materials and methods” part.

Minor Comments:

The data as presented is convincing, and the evidence for the role of MYSM1 as a co-activator of ER-alpha is extensive. Given the amount of data, I do not believe any additional experiments are needed. I could not find any description of ethics for the patient samples used.

• Response: Appreciate for the positive response from the reviewer. According to the important suggestions, the ethics approval for the patient specimens have been included in the “Materials and methods” part.

  (1)- Figure 4C - is the increase of binding in response to Estrogen significant? It is an important control to show for MCF7 as Fig 4B is in T47D.

Response: According to the comments from reviewers, we conducted statistical difference analysis in Figure 4C, our results have shown that the recruitment of MYSM1 or ERa on c-Myc ERE region is significantly increased upon E2 treatment in MCF-7 cells.

*(2)- Figure 6 - Can we clarify that B = Before, A = After *

Response: Apologize for the unclear description in Figure 6. As clarified by the reviewer, “B” represents before AI treatment, “A” represents after AI treatment. We have included the description in the “Figure legends” section.

(3)- The use of Fig EV was confusing to me, I assume it means supplementary?

Response: Thank you for your question. Since our priority affiliate journal is belong to EMBO Press, this manuscript was written according to the relevant requirements and “EV” is the abbreviation of “Expanded View”, which is the same as that of the supplementary figures.

Reviewer #1 (Significance (Required)): - Discovery science to understand the regulation of the ER is critical in discovering new opportunities to target breast cancer. As far as I can tell this is the first study where MYSM1 is a co-regulator of the ER. - The significance would be greatly increased if the manuscript identified opportuinities to target the ER via this pathway using existing compounds. However, it is reasonable to consider this is beyond the scope of this study.

Response: According to your valuable suggestion, we thus turned to screen the commercially-available compound in ZINC database to find the compounds that could spatially interact with MYSM1 protein, thereby inhibiting the activity of MYSM1. We plan to perform the additional biological function experiments to explore the effect of MYSM1-targeting compounds on the sensitivity of breast cell lines to anti-estrogen treatment.

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

*Below I outline a few suggestions that can help clarify specific aspects of the study. *

Fig. 2: Ideally a rescue study with a wild-type and catalytically mutant MYSM1 should be performed.

Response: Thank you for your suggestion. To address this point, we will perform a rescue study with a wild-type and catalytically mutant MYSM1 in the breast cancer cells with stable knocked down of MYSM1 to examine the corresponding protein expression of ERa target genes.

What is the ERa interactome in the presence and absence of MYSM1? Proteomics studies upon shMYSM1 should be performed. Alternatively, a better characterization of ERa-containing complexes upon shMYSM1 should be performed.

Response: We agree with the reviewer’s suggestion to functionally address the influence of MYSM1 on ERa interactome. In breast cancer cells with the presence or absence of MYSM1, Co-IP experiments will be conducted to examine the influence of MYSM1 on the interaction between ERa and KAT2B, EP300 and CREBBP complex, which are predicted from String database.

*Fig. 3: Does MYSM1 control its own protein via deubiquitination? *

Response: We thank the reviewer for this suggestion and it provides us with a novel perspective upon MYSM1 investigation of whether MYSM1 is the deubiqutination substrate of itself. We would first transfect MYSM1-FL or MYSM1-ΔMPN plasmids and detect whether the endogenous MYSM1 expression changes. Next step, ubiquitination assays will be performed to determine whether MYSM1 control its own protein via deubiquitination.

*Fig. 4: I propose that the authors perform MYSM1 ChIP-Seq to better show the MYSM1 distribution and overlap with ERa distribution. *

Response: Appreciate for the reviewer for the valuable and important comments. ChIP-seq will be additionally performed in MCF-7 cells with MYSM1 antibody to examine the MYSM1 occupation on global chromatin in response to E2 and to show its overlap with ERa distribution.

Fig. 7. Is there a correlation between MYSM1 mRNA and protein levels in cancer and physiological samples? How is the MYSM1 transcriptionally regulated in physiological and cancer cells?

Response: We thank the reviewer for raising this issue. We will detect MYSM1 mRNA and protein levels in breast cancer and physiological samples, along with physiological and breast cancer cells. Statistics for MYSM1 transcriptional level will be further displayed.

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

*Luan et al performed a detailed analysis on the potential coactivator MYSM1 and its role in regulating the expression of ER and ER-dependent genes by being a deubiquitinase of ER as well the repressive mark, H2Aub1. This study has demonstrated an excellent work on the biochemistry aspect of the story with meticulous work on the role of specific domains of MYSM1 and ER and how they interact and how the deubiquitination process is regulated. This was identified initially in Drosophila models, but eventually and promptly explored in multiple breast cancer cell lines and patient samples. *

*Major Comments: *

1. • It is really exciting to see how MYSM1 regulates ER activity and it looks like expression of ER is the first event of regulation by MYSM1's. However, H3Ac would be the very intermediate event of ER activity. This brings a question of whether ER complex itself is affected by MYSM1 - for example, does MYSM1 affect p300, SWI/SNF and other ER-associated coactivator binding? Does it affect chromatin accessibility? Which exact histone mark of H3Ac is affected, as different proteins are involved in the acetylation of histones. *

Response: Appreciate the reviewer for the valuable questions. The Co-IP and ChIP experiments will be conducted respectively to assess the influence of MYSM1 on the binding of ERa with its associated co-activators and their recruitments on EREs upon MYSM1 knockdown. In addition, ChIP assays will also be performed to determine the effect of MYSM1 on histone modification levels (H3K9ac, H3K27ac, et al). MNase assay will be further performed to examine the function of MYSM1 on chromatin accessibility.

• The regulation of MYSM1 is mainly shown on promoters of ER regulated genes. However, ER primarily bind to enhancers. Is there any general effect on enhancers? *

Response: Thank you for your comments. We will perform ChIP assays to detect the regulation of MYSM1 on ERa binding to enhancers of ERa regulated genes in breast cancer cells.

3. MYSM1 is not the complex usually cells prefer to deubiquitinate H2Aub, but BAP1. What is the role of BAP1 here? Are they redundant or any cross-talk?

Response: Concerning this interesting question, it has been reported that BAP1 co-activator function correlated with increased H3K4me3 and concomitant deubiquitination of H2Aub at target genes. However, BAP1 has not been reported as an ERa co-regulator so far. Moreover, the interaction between ERa and BAP1 cannot be predicted using the STRING database. Whether BAP1 plays a similar role as MYSM1 in breast cancer and how MYSM1 cooperates with the other DUBs to regulate the genome-wide landscape of histone H2A ubiquitination and the gene expression profiles of different mammalian cell types remains to be elusive. It would be necessary to further study in the future.

• Effect of MYSM1 on histone marks on the EREs - only one ERE is shown. Multiple EREs should be validated by qPCR. Enhancers should also be focused. Does it affect H3K27ac or H3K4me1?*

Response: Thank you for your suggestions. ChIP experiments will be conducted to examine the effect of MYSM1 on histone marks on multiple EREs of ERa target genes. Furthermore, we will focus on the effect on MYSM1 on hitone marks (H3K27ac and H3K4me1 levels, et al) on enhancers of ERa target genes.

• It is clear that MYSM1 is required for the response to antiestrogen therapies. However, the link to resistance is not completely clear. This should be investigated with multiple Tamoxifen resistant cell lines. There is one cell line used, but it is responding to tamoxifen even at lower concentrations in Crystal violet assays. MYSM1 overexpression in nonresponders doesn't mean that their activity is also more. Binding analyses should be analysed in proper Tamoxifen-resistant cell lines. Usually, Tamoxifen is used or works at concentrations from 100 nM - 1 uM in vitro to see the transcriptional effects. However, the authors claim that these are very high concentrations, but actually they aren't the concentrations which promote toxicity.*

Response: We thank reviewer for the valuable comments. According to your suggestion, we will construct Tamoxifen-resistant MCF-7 or T47D cell lines carrying stable knockdown of MYSM1 to perform the biological function experiments with appropriate Tamoxifen concentrations to further confirm the effect of MYSM1 on the sensitivity of cells to anti-estrogen. In addition, we will examine the expression of MYSM1 and ERa target genes or histone H2Aub levels in nonresponders samples to preliminarily determine the activity of MYSM1 in AI-resistant samples.

• Discussion about DUB inhibitors - how specific are these? Would they be useful to target MYSM1 activity and thus ER regulation in nonresponders or resistant cell lines? This would add up strongly on the clinical potential of the study. *

Response: The DUB inhibitors mentioned in discussion are specific to USP14 and UCHL5, but not MYSM1. We thus turned to screen the commercially-available compound in ZINC database to find the compounds that could spatially interact with MYSM1 protein, thereby inhibiting the activity of MYSM1. We plan to perform the additional biological function experiments to explore the effect of MYSM1-targeting compounds on the sensitivity of breast cell lines to anti-estrogen treatment.

• OPTIONAL: ChIP-seq analyses on the factors would be more informative to look at the unbiased mechanisms including enhancers. *

Response: We appreciate your important comments. We plan to perform ChIP-seq in MCF-7 cells with MYSM1 antibody to examine the MYSM1 occupation on global chromatin in response to E2 and to show its overlap with ERa distribution.

• Number of replicates aren't clear in figure legends. Are they biological or technical replicates?*

Response: We thank for your comments. We have included the number of replicates in the “materials and methods” and “Figure legends” sections.

*Minor comments: *

• Please give page numbers and line numbers in the manuscript.*

Response: We have given page numbers and line numbers in the revised manuscript.

• Title - "MYSM1 co-activates ER action". "Action" is not needed to be mentioned here.*

Response: We have modified the title according to the reviewer’s suggestion. The title has been modified as below: “MYSM1 acts as a novel co-activator of ERα via histone and non-histone deubiquitination to confer antiestrogen resistance in breast cancer”.

• Abstract talks about the work on Drosophila mainly, but apart from the first experiment, everything else is done on mammalian cell culture and also clinically relevant patient samples. *

Response: Thank you for your important comments. We have modified the abstract contents with breast cancer-derived cell lines instead of Drosophila experimental system.

• Abstract Line 13 - the work is done many ER regulated genes and not gene.*

Response: We've modified the text into “ERa-regulated genes” in Abstract section.

• Pg 6 first paragraph - What/how many mutants were screened here? *

Response: Thank you for your suggestion. In this study, about 300 fly lines carrying loss of function mutants obtained from Bloomington Stock Center were used for screening.

• CoIP protocol is not clear. It says followed with manufacturer instructions but no kit information is provided.*

Response: Apologize for the misrepresentation. Co-IP experiments were performed as that in the previous study. We have corrected the description for CoIP protocol and cited our previous study in the Materials and Methods section.

• Fig. 1H, etc - can you show a zoomed in or DAPI removed (from merge) picture to show the interactions clearly? It's hard to follow the yellow co-interaction spots as they are hidden behind the blue colour. Any kind of quantification analyses would be wonderful.*

Response: Thank you for your suggestion, we have merged the red and green colours to precisely show the co-location of MYSM1 and ERa.

• Fig. EV1H - can you link this with the results from Fig. 1F to discuss if the delta SANT-MYSM1 lost the interaction with ER also in the IF studies? *

Response: Thank you for your question. Commonly, the fluorescence intensity of confocal results mainly represents the amount of ectopic expression of MYSM1 or ERa, Co-IP experiments more exactly represent the association between proteins. It would be better to pick up the similar cell number in confocal experiments to assess the intensity of protein interaction. We will repeat the confocal again to show the exact fluorescence intensity.

• Pg 7 - 3-4th line from last - These lines should move above where AF1 and AF2 are introduced. According to Fig. 1G, the interaction of AF2 and MYSM1 is important. Why do we see an effect on AF1 as well in Fig. 2B?*

Response: Thank you for your comments. The GST ERa-AF1 and GST ERa-AF1 fusion proteins contain 29-180aa and 282-595aa of ERa truncated mutants respectively, while the ERa-AF1 and ERa-AF2 expression plasmids used in luciferase assay in Fig 2B encode 1-282aa and 178-595aa fragments. We can see the ERa-AF1 mutant in Fig 2B contains more amino acid segments than that in GST ERa-AF1 in Fig. 1G. We speculate that MYSM1 may interact with the extra segment (180aa-282aa) to upregulate ERa-AF1 induced transcription. To make it clear, we have included relevant description in the text along with a schematic representation of ERa, ERa-AF1, and ERa-AF2 plasmids used in luciferase reporter assays in Fig EV2B and in materials and methods section.

• It's confusing to have HEK and breast cancer cell line datasets swapped inconsistently between main figures and Supplementary figures. It would be nice to keep them consistent. *

Response: We have reverse the order of Fig 2B and Fig EV2C to maintain the consistency of the cell line datasets.

• RPMI is spelled wrong in Pg. 19. *

Response: We have corrected the spelling error of RPMI.

• How long is the estrogen treatment done in each experiment? What is the concentration? This should be mentioned in the figure legends. 12 or 24 hrs time point is a later stage of estrogen receptor induction. Even 1-3 hrs would be sufficient to promote a stronger effect on RNA transcription than that of these later time points. What you are looking at is all effect on later time points and the effect should be observed on earlier time points to observe dynamic and immediate effects. p-values are required for the comparison on no E2 vs E2 here.*

Response: We appreciate your valuable comment. We have rephrased the description on estrogen treatment in “Material and methods” and “Discussion” parts to more clearly state that E2 (100nM) was given for 4-6h in the experiments detecting transcriptional levels, while 16-18h in the experiments detecting translation levels. In addition, p-values have included to display the change of MYSM1 and ERa recruitment on ERE region upon E2 treatment.

• Fig. 2G - effect on c-Myc after MYSM1 knockdown is not clear comparing to the previous WB in 2E.*

Response: We will replace a clear image in Fig 2G to show the change of c-Myc protein expression after MYSM1 knockdown.

• Pg. 8 - start of the last paragraph - "Unexpectedly, in Co-IP experiment as shown in Figure 2E and F" - These are not Co-IP experiments. *

Response: Apologize for the writing error. We have re-written the sentence “Unexpectedly, in western blot experiments as shown in Figure 2E and F” in line 229.

• Fig. 3C and E - Quantification with comparison needed.*

Response: Relative ERa levels were semi-quantified by densitometry and normalized by the relative expression of 0 hour to compare the ERa degradation rate in Fig 3C and E.

• Pg 10 - subtitle - multiple gene promoters have been looked, but the subtitle says "gene". Only ERE for c-MYC is looked at, but it says EREs.*

Response: We have modified the word “genes” and “ERE” in correct forms in the text.

• MYSM1 is in the nucleus in IF even before E2 treatment, however it is recruited after estrogen treatment in ChIP assays. Explain why there is a difference seen here. What other targets they might bind to in the nucleus?*

Response: The aim of ChIP experiments is to examine the recruitment of MYSM1 protein on the DNA in the presence of E2, while IF results represent the MYSM1 subcellular distribution in the nucleus even in the absence of E2. MYSM1 has been reported to bind to promoters of numerous target genes, including Ebf1 in B cell progenitors, Pax5 in naïve B cells, miR150 in B1a cells, Id2 in NK cell progenitors, Flt3 in dendritic cell precursors, and Gfi1 in hematopoietic stem and progenitor cells. In our study, we plan to perform ChIP-seq to further show its potential binding elements on the global genome in ER-positive breast cancer.

• Pg. 10 last line - the sentence should be combined with comma.*

Response: Thank you for pointing this out, we have combined a comma in the sentence.

• Fig. 5H - What about Ki67 which is a proliferative marker for cancer cell growth?*

Response: We will further perform IHC experiments to compare Ki67 expression in the shCtrl and shMYSM1 group of xenograft tumors from nude mice.

• Pg 12 - Samples were used from patients treated with AI adjuvant treatment. A small summary of details are needed here including n, arm, details of administration, etc even though mentioned in Methods.*

Response: We have restated the patients’ condition and administration details in lines 342-250.

• MYSM1 is upregulated in nonresponders, but it is also downregulated in responders which is ignored. What would this mean mechanistically? Don't patients need MYSM1 for the response or after treatment? Does estrogen inhibition regulate MYSM1 upstream? *

Response: Appreciate for your important questions. The changes of intracellular environment caused by AI treatment are complicated and varied. The mechanism underlying such a phenomenon is largely unclear. We plan to perform western blot and ubiquitination assays to compare the expression and activity of MYSM1 in endocrine-resistant breast cancer cells treated or untreated with endocrine drugs to identify the effects of estrogen inhibition on MYSM1 expression. Moreover, we will detect whether MYSM1 expression is correlated with cell cycle and cell proliferation states.

• Pg 13 - Is this data associated with any trial? More details are needed. *

Response: We appreciate for your helpful comment. We have rearranged the logic of the article in order to clarify our reasoning for presenting this data. The modified contents included in lines 367-371 in the modified version are followed below: The regulation of MYSM1 on ERa action indicates that MYSM1 acts as a novel ERa co-activator, suggesting that MYSM1 may play an important role in breast cancer. We then conducted western blot and IHC experiments to estimate MYSM1 expression and the correlation between MYSM1 expression and clinicopathologic factors of the patients.

• Last lines of Pg 15 - These were already introduced in the results. *

Response: We thank reviewer for their highlighting this redundancy in our text. We have simplified the text in lines 442-444.

• Pg 16 - third last line of the first paragraph - makes typo.*

Response: Thanks for pointing out this typo. We have corrected the word “make” in line 456.

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Referee #3

Evidence, reproducibility and clarity

Luan et al performed a detailed analysis on the potential coactivator MYSM1 and its role in regulating the expression of ER and ER-dependent genes by being a deubiquitinase of ER as well the repressive mark, H2Aub1. This study has demonstrated an excellent work on the biochemistry aspect of the story with meticulous work on the role of specific domains of MYSM1 and ER and how they interact and how the deubiquitination process is regulated. This was identified initially in Drosophila models, but eventually and promptly explored in multiple breast cancer cell lines and patient samples.

Major Comments:

1. It is really exciting to see how MYSM1 regulates ER activity and it looks like expression of ER is the first event of regulation by MYSM1's. However, H3Ac would be the very intermediate event of ER activity. This brings a question of whether ER complex itself is affected by MYSM1 - for example, does MYSM1 affect p300, SWI/SNF and other ER-associated coactivator binding? Does it affect chromatin accessibility? Which exact histone mark of H3Ac is affected, as different proteins are involved in the acetylation of histones.
2. The regulation of MYSM1 is mainly shown on promoters of ER regulated genes. However, ER primarily bind to enhancers. Is there any general effect on enhancers?
3. MYSM1 is not the complex usually cells prefer to deubiquitinate H2Aub, but BAP1. What is the role of BAP1 here? Are they redundant or any cross-talk?
4. Effect of MYSM1 on histone marks on the EREs - only one ERE is shown. Multiple EREs should be validated by qPCR. Enhancers should also be focused. Does it affect H3K27ac or H3K4me1?
5. It is clear that MYSM1 is required for the response to antiestrogen therapies. However, the link to resistance is not completely clear. This should be investigated with multiple Tamoxifen resistant cell lines. There is one cell line used, but it is responding to tamoxifen even at lower concentrations in Crystal violet assays. MYSM1 overexpression in nonresponders doesn't mean that their activity is also more. Binding analyses should be analysed in proper Tamoxifen-resistant cell lines. Usually, Tamoxifen is used or works at concentrations from 100 nM - 1 uM in vitro to see the transcriptional effects. However, the authors claim that these are very high concentrations, but actually they aren't the concentrations which promote toxicity.
6. Discussion about DUB inhibitors - how specific are these? Would they be useful to target MYSM1 activity and thus ER regulation in nonresponders or resistant cell lines? This would add up strongly on the clinical potential of the study.
7. OPTIONAL: ChIP-seq analyses on the factors would be more informative to look at the unbiased mechanisms including enhancers.
8. Number of replicates aren't clear in figure legends. Are they biological or technical replicates?

Minor comments:

1. Please give page numbers and line numbers in the manuscript.
2. Title - "MYSM1 co-activates ER action". "Action" is not needed to be mentioned here.
3. Abstract talks about the work on Drosophila mainly, but apart from the first experiment, everything else is done on mammalian cell culture and also clinically relevant patient samples.
4. Abstract Line 13 - the work is done many ER regulated genes and not gene.
5. Pg 6 first paragraph - What/how many mutants were screened here?
6. CoIP protocol is not clear. It says followed with manufacturer instructions but no kit information is provided.
7. Fig. 1H, etc - can you show a zoomed in or DAPI removed (from merge) picture to show the interactions clearly? It's hard to follow the yellow co-interaction spots as they are hidden behind the blue colour. Any kind of quantification analyses would be wonderful.
8. Fig. EV1H - can you link this with the results from Fig. 1F to discuss if the delta SANT-MYSM1 lost the interaction with ER also in the IF studies?
9. Pg 7 - 3-4th line from last - These lines should move above where AF1 and AF2 are introduced. According to Fig. 1G, the interaction of AF2 and MYSM1 is important. Why do we see an effect on AF1 as well in Fig. 2B?
10. It's confusing to have HEK and breast cancer cell line datasets swapped inconsistently between main figures and Supplementary figures. It would be nice to keep them consistent.
11. RPMI is spelled wrong in Pg. 19.
12. How long is the estrogen treatment done in each experiment? What is the concentration? This should be mentioned in the figure legends. 12 or 24 hrs time point is a later stage of estrogen receptor induction. Even 1-3 hrs would be sufficient to promote a stronger effect on RNA transcription than that of these later time points. What you are looking at is all effect on later time points and the effect should be observed on earlier time points to observe dynamic and immediate effects. p-values are required for the comparison on no E2 vs E2 here.
13. Fig. 2G - effect on c-Myc after MYSM1 knockdown is not clear comparing to the previous WB in 2E.
14. Pg. 8 - start of the last paragraph - "Unexpectedly, in Co-IP experiment as shown in Figure 2E and F" - These are not Co-IP experiments.
15. Fig. 3C and E - Quantification with comparison needed.
16. Pg 10 - subtitle - multiple gene promoters have been looked, but the subtitle says "gene". Only ERE for c-MYC is looked at, but it says EREs.
17. MYSM1 is in the nucleus in IF even before E2 treatment, however it is recruited after estrogen treatment in ChIP assays. Explain why there is a difference seen here. What other targets they might bind to in the nucleus?
18. Pg. 10 last line - the sentence should be combined with comma.
19. Fig. 5H - What about Ki67 which is a proliferative marker for cancer cell growth?
20. Pg 12 - Samples were used from patients treated with AI adjuvant treatment. A small summary of details are needed here including n, arm, details of administration, etc even though mentioned in Methods.
21. MYSM1 is upregulated in nonresponders, but it is also downregulated in responders which is ignored. What would this mean mechanistically? Don't patients need MYSM1 for the response or after treatment? Does estrogen inhibition regulate MYSM1 upstream?
22. Pg 13 - Is this data associated with any trial? More details are needed.
23. Last lines of Pg 15 - These were already introduced in the results.
24. Pg 16 - third last line of the first paragraph - makes typo.

Significance

• The study seems to be novel as MYSM1 is never studied before as a coactivator for ER. This expands the wealth of knowledge we have on coactivators which can be explored for its potential targeting to treat advanced breast cancers. The study seems to be support the biochemical aspects of ER interaction, but vaguely uncovers the functional or epigenetic mechanisms.
• Studies on coactivators/coregulators of ER is very important, as modulating ER alone is not efficient enough to solve the puzzle of antiestrogen resistance. The expression/activity levels of the coregulators are very important as these can be modulated in cancers due to epigenetic reprogramming during resistance and mutations on these genes dominate. They can also serve as potential targets especially when cells don't respond to classical ER targeting therapies.
• Strength - Biochemical analyses of the interactions and detailed mechanistic information
• Limitation - Studies are very much limited to the biochemical regulation on ER and not on the molecular or epigenetic mechanisms. Association of MYSM1 in resistance mechanisms isn't clear.
• Audience - this can be interesting for both basic research and clinical audience. Biochemical knowledge would help people to understand how a nonclassical deubiquitinase can promote nuclear receptor associated transcription by targeting genomic and nongenomic targets simultaneously. Clinically this study would be relevant if the MYSM1-ER interaction can be targeted using DUB inhibitors, as requested.
• Area of expertise of the reviewer - breast cancer, nuclear receptors, estrogen receptor biology, epigenetics, bioinformatics

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Referee #2

Evidence, reproducibility and clarity

Below I outline a few suggestions that can help clarify specific aspects of the study.

Fig. 2: Ideally a rescue study with a wild-type and catalytically mutant MYSM1 should be performed. What is the ERa interactome in the presence and absence of MYSM1? Proteomics studies upon shMYSM1 should be performed. Alternatively, a better characterization of ERa-containing complexes upon shMYSM1 should be performed.

Fig. 3: Does MYSM1 control its own protein via deubiquitination?

Fig. 4: I propose that the authors perform MYSM1 ChIP-Seq to better show the MYSM1 distribution and overlap with ERa distribution.

Fig. 7. Is there a correlation between MYSM1 mRNA and protein levels in cancer and physiological samples? How is the MYSM1 transcriptionally regulated in physiological and cancer cells?

Significance

This is a very comprehensive study characterizing the role of MYSM1 deubiquitinase in ERa transcriptional programs in breast cancer systems. Breast cancer therapy is an unmet need and the role of deubiquitinases warrants further investigation. This accounts for the high significance of the story.

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Referee #1

Evidence, reproducibility and clarity

Summary:

ER+ breast cancer is the most common form of cancer. Targeting ER-alpha transcriptional cofactors present one potential method to target the disease. The authors demonstrate that MYSM1 is a histone deubiquitinase and a novel ER cofactor, functioning by up-regulating ER action via histone deubiquitination.

Loss of MYSM1 attenuated cell growth and increase breast cancer cell lines' sensitivity to anti-estrogens. The authors, therefore, propose MYSM1 as a potential therapeutic target for endocrine resistance in Breast cancer.

Major Comments:

• The data as presented is convincing, and the evidence for the role of MYSM1 as a co-activator of ER-alpha is extensive.
• Given the amount of data, I do not believe any additional experiments are needed.
• I could not find any description of ethics for the patient samples used.

Minor

• Figure 4C - is the increase of binding in response to Estrogen significant? It is an important control to show for MCF7 as Fig 4B is in T47D.
• Figure 6 - Can we clarify that B = Before, A = After
• The use of Fig EV was confusing to me, I assume it means supplementary?

Significance

• Discovery science to understand the regulation of the ER is critical in discovering new opportunities to target breast cancer. As far as I can tell this is the first study where MYSM1 is a co-regulator of the ER.
• The significance would be greatly increased if the manuscript identified opportuinities to target the ER via this pathway using existing compounds. However, it is reasonable to consider this is beyond the scope of this study.

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Reply to the reviewers

We apologize for the delay in resubmitting this revised manuscript. We faced a number of challenges over the previous year unrelated to this project that slowed progress on completing the necessary revisions. However, we are happy to report we have addressed all of the reviewer’s valuable comments in this revised submission through the including of 27 new or improved figure panels and significant adaptations to the text. We highlight these changes below.

REVIEWER #1.

Reviewer #1 General Comments. “This study investigates changes in mitochondrial morphology in response to ER stress due to pharmacological inhibition or genetic dysfunction in vitro via two different cell models (MEFs and HeLa cells). The authors specifically implicate the PERK branch of the ER-stress induced pathway in this process based on the observation that mitochondria elongate in response to thapsigargin (Tg) treatment which is blocked by the pathway inhibitors GSK and ISRIB or by genetic ablation of Perk/PERK. Homozygous knockout cells lacking PERK exhibit a fragmented mitochondrial phenotype even in the absence of Tg, which is rescued by expression of the wildtype but not a hypomorphic allele (PERKPSP). One of the more interesting suppositions of this manuscript is that mitochondrial elongation is dependent on the abundance of phosphatidic acid (PA); treatment with Tg provokes an increase in mitochondrial PA, but PA does not accumulate in mitochondria from cells co-treated with GSK, an inhibitor of PERK. This correlation suggests that increased mitochondrial PA accumulation is PERK-dependent. In addition, predicted manipulation of PA levels achieved by a gain of function expression of the lipase Lipin diminished mitochondrial elongation in response to ER stress. Similar results were obtained by PA-PLA1 overexpression, a cytosolic lipase that converts PA into lysophosphatidic acid (LPA). To further describe the mechanistic link between ER stress and mitochondrial morphology, the authors found that PRELID1, which transports PA from the OMM to the intermembrane space, and TIM17A, a component of the protein translocation machinery, were stabilized by loss of PERK or YME1L [and possibly an effect of ATF4], regardless of ER stress via Tg treatment. The authors also report that Tg treatment prevents OPA1 cleavage in cells treated with CCCP, an uncoupler of the proton gradient, suggesting that the effect due to Tg treatment is not through ER stress but decreased mitochondrial fusion via mito-stress induced OPA1 cleavage. To address this, cells were treated with ionomycin which induces mitochondrial fragmentation independent of DRP1. The authors observed an increase in mitochondrial fragmentation in the presence of ionomycin. However, co-treatment with Tg prevented fragmentation, as did overexpression of mitoPLDGFP, which converts cardiolipin to PA on the OMM. These results support a model in which, under ER stress conditions, PERK activation leads to translational attenuation, which leads to a decrease in the steady state levels of PRELID1 via YME1L-dependent degradation and to the accumulation of PA on the OMM. Based on published work this PA accumulation is expected to inhibit the mitochondrial division dynamin, DRP1. The authors tested this by examining the dependence of mitochondrial elongation on PRELID1.”

“Perturbances in PERK signaling evoke an alteration in mitochondrial morphology and have been extensively reported on, due to their clinical implications on neurodegenerative disorders such as Alzheimer's disease. The present work provides insight into the molecular basis for Stress Induced Mitochondrial Hyperfusion (SIMH) which can be triggered by ER stress. The authors find that this process occurs downstream of PERK and proceeds through accumulation of PA in the OMM by stabilization of Prelid, a mitochondrial resident protein that transports PA from the OMM to IMM for cardiolipin synthesis. The evidence of this work represents a substantial addition to the field of mitochondrial dynamics/SIMH and the Unfolded Protein Response”

“The novelty of this work is in the inclusion of PRELID1 downstream of PERK signaling pathway for transmission of ER stress to the mitochondria, a process that involves phosphatidic acid (PA). Some studies have addressed how phosphatidic acid is a modulator and a signal in mitochondrial physiology. The role of the lipids in mitochondrial dynamics represent an important and emerging field that needs to be explored in order to understand how metabolites control mitochondrial fusion/fission.”

__Our Response to Reviewer #1 General Comments. __We thank the reviewer for the positive comments related to our manuscript. We address specific comments brought up by the reviewer in our revised manuscript as highlighted below. We combined specific comments related to the same point in this response to best manage the various points brought up by the reviewer.

Reviewer #1 Comment #1. __The Reviewer__ brought up the quality of our images numerous times in their review. A few examples are included below.

“Image quality of mitochondria is sub par and the images do not always appear representative of/match the accompanying histograms. When using a single fluorescent marker (mito-GFP), the images should be in grey scale.”

“In several images there is substantial background GFP signal resulting in images that are fuzzy on the high quality PDF (printout is unintelligible). Example: Figure 2, Mock+veh. Example: Figure S2I, Mock+veh, +PA-PLA Tg. Example: Figure 3C mock+veh”

“Images from prior paper (Lebeau J, et al. 2018) are of much higher quality and is much easier to discern mitochondrial”

“Mitochondrial morphology doesn't appear uniform even within the same cell so how is this accounted for in scoring of mitochondrial morphology? Also, how are authors scoring mitochondrial morphology? Due to the inconsistencies in the chosen images, we feel this manuscript would benefit from addition of a supplementary figure showing examples for each cell model expressing mtGFP (i.e. HeLa and MEFs) depicting the fragmented, tubular and elongated mitochondria. This should be able to be constructed from images already collected for these analyses that weren't already used in the paper.”

__Our Response to Reviewer #1 Comment #1. __In the revised manuscript, we improved the quality of the images and converted all images to greyscale, as suggested by the reviewer.

As described in Materials and Methods, we quantified mitochondrial morphology by cell, scoring whether a cell has primarily fragmented, tubular, or elongated mitochondria morphology. This scoring was performed by at least two blinded researchers for at least 3 independent experiments with a total of >60 cells/condition counted across all experiments. Scores for individual experiments were then combined and averaged. Statistics were calculated from these averaged scores. In the revised manuscript, the images presented are representative of each individual condition. In addition, we now include new panels showing the quantification of total cells counted/condition across all individual replicates by a representative researcher for the main text figures (e.g., see Fig. S1C). This provides an alternative representation of the observed phenotype across the individual experiments for these key figures.

As suggested by the reviewer, in the revised submission we also now provide representative images of cells with primarily fragmented, tubular, and elongated mitochondria for both MEF and HeLa cells (Fig. S1A,B). We appreciate this suggestion as we feel it improves the clarity of our manuscript.

Reviewer #1 Comment #2. ____“Mitochondria in Perk-/- MEFs are highly fragmented, which is potentially inconsistent with previous work (Lebeau J, et al. 2018) performed by the same research group. Can the authors comments on this discrepancy? Also, do the authors interpret this fragmentation to mean that Perk is required to maintain mitochondrial elongation in the absence of exogenous ER stress (Tg)? If so, the authors should test whether expression of a dominant negative version of DRP1 rescues this fragmented morphology. This would be an additional critical test of the authors' model.”

“Vehicle treated Perk-/- cells have fragmented morphology which is different from Figure 2F in above publication by same group. Can the authors explain this discrepancy?”

Our Response to Reviewer #1 Comment #2. In our previous publication, we did not quantify mitochondrial morphology in Perk-deficient cells. However, as reported in this current manuscript, we find that Perk-deficient cells display higher amounts of fragmented mitochondria, as compared to Perk+/+ MEFs (Fig. 1B,C). We quantified this result across 5 independent experiments. Moreover, we found that reconstitution with PERKWT restored tubular mitochondrial morphology in Perk-deficient cells, demonstrating that this effect can be attributed to loss of PERK.

With respect to the increase in mitochondrial fragmentation observed in Perk-deficient MEFs, we attribute this to reduced mitochondrial membrane potential observed in these cells. We now show that Perk-deficient MEFs show 50% reductions in TMRE staining, as compared to controls. We include this data in the revised manuscript as __Fig. S1D __and the accompanying text below.

Line 91. “*Perk-/- MEFs showed increases in fragmented mitochondria in the absence of treatment (Fig. 1B,C and Fig. S1C). This corresponds with reductions in the mitochondrial membrane potential in Perk-deficient cells, as measured by tetramethylrhodamine ethyl ester (TMRE) staining (Fig. S1D). This suggests that the increase of fragmentation in these cells can be attributed to mitochondrial depolarization. Tg-induced mitochondrial elongation was also impaired in Perk-deficient cells (Fig. 1B,C and Fig. S1C).”. *

Reviewer #1 Comment #3. “The authors postulate that mitochondrial elongation in response to Perk activation is specifically outer membrane PA-dependent negative regulation of DRP1. However, PA is readily convertible to other phospholipids, notably CL and LPA, both of which positively regulate mitochondrial fusion. The authors do not measure abundance of other phospholipids, particularly LPA or CL in their targeted lipidomics experiments, only PC. The authors need to consider this alternate possibility.”

Reviewer #1 Comment #3. __Overexpression of PA-PLA1 (which converts PA to LPA) blocks ER stress induced mitochondrial elongation (__Fig. S2L-O). This indicates that the observed Tg-dependent increase in mitochondrial elongation are unlikely to be attributed to increases in LPA. mitoPLD converts CL to PA at the outer mitochondrial membrane. Since mitoPLD overexpression increases mitochondrial elongation (Fig. 3A,B), this again suggests that CL is not a major driver of mitochondrial elongation. These results combined with the sensitivity of ER stress induced mitochondrial elongation to two different PA lipases strongly support a model whereby increases in PA contribute to ER stress induced mitochondrial elongation.

In the revised manuscript, we include measurements of CL in mitochondria isolated from MEFmtGFP cells treated with Tg and/or depleted of Prelid1. As expected, reductions of PRELID1 decrease CL in isolated mitochondria (Fig. S5C). Treatment with Tg reduced CL to similar extents in mitochondria isolated from MEFmtGFP cells expressing non-silencing shRNA. However, we did not observe further reductions of CL in Prelid1-depleted cells. This is consistent with a model whereby ER stress-dependent reductions in PRELID1 decrease PA trafficking across the IMS and lead to reductions in CL synthesis. These results are discussed in the revised manuscript as below:

Line 214. “PRELID1 traffics PA from the outer to inner mitochondrial membrane, where it serves as a precursor to the formation of cardiolipin.56,66,67 Thus, reductions in PRELID1 should decrease cardiolipin. To test this, we shRNA-depleted Prelid1 from MEFmGFP cells and monitored cardiolipin in isolated mitochondria in the presence or absence of ER stress. We confirmed efficient PRELID1 knockdown by immunoblotting (Fig. S5A). Importantly, Prelid1 depletion did not alter Tg-induced reductions of TIM17A or increases of ATF4. Further, Tg-dependent increases in PA were observed in Prelid1-depleted MEFmtGFP cells (Fig. S5B). These results indicate that loss of PRELID1 does not impair PERK signaling in these cells. Prelid1 depletion reduced cardiolipin in mitochondria isolated from MEFmtGFP cells (Fig. S5B). Treatment of MEFmtGFP cells expressing non-silencing shRNA with Tg for 3 h also reduced cardiolipin to levels similar to those observed in Prelid1-deficient cells. However, Tg did not further reduce cardiolipin in Prelid-depleted cells. These results are consistent with a model whereby ER stress-dependent reductions in PRELID1 limit PA trafficking across the inner mitochondrial membrane and contribute to reductions in cardiolipin during acute ER stress”

Reviewer #1 Comment #4. “In Figure 5, the authors found very little difference in mitochondrial elongation following knockdown of Prelid1 (comparison between vehicle only conditions), which is potentially inconsistent with their model as decreased PRELID1 should lead to increased OMM PA [and subsequently mitochondrial fusion/elongation]. Therefore, these findings do not adequately support the authors' main model.”

Our Response to Reviewer #1 Comment #4. __Our model predicts that ER stress induced mitochondrial elongation is mediated through a process involving both PERK kinase-dependent increases in total PA and YME1L-dependent PRELID1 degradation induced downstream of PERK-dependent translation attenuation (see __Fig. 6). Thus, we predict that PRELID1 degradation is required, but not sufficient, to promote mitochondrial elongation. Our results showing that PRELID1 depletion does not basally disrupt mitochondrial morphology or inhibit Tg-induced mitochondrial elongation are consistent with this model. Moreover, we show that genetic Prelid1 depletion rescues Tg-induced mitochondrial elongation in cells co-treated with the PERK signaling inhibitor ISRIB – a compound that blocks PERK-dependent PRELID1 degradation (Fig. 4D), but not increases in PA (Fig. 2B, S2E,F) – in both MEFmtGFP and HeLa cells (Fig. 5A-D). This is consistent with our proposed model whereby PRELID1 degradation is required but not sufficient for promoting mitochondrial elongation. We make this point clearer in the revised manuscript.

Line 259: “Interestingly, Prelid1 depletion did not basally influence mitochondrial morphology or inhibit Tg-induced mitochondrial elongation (Fig. 5A,B and Fig. S5E). This indicates that reduction of PRELID1, on its own, is not sufficient to increase mitochondrial elongation, likely reflecting the importance of PERK kinase-dependent increases in PA in this process.53”

Reviewer #1 Comment #5. “The manuscript requires more careful editing - there were grammatical and punctuation errors.”

“… the text needs considerable editing to make the language clearer and formal whereas the figures are not always presented in a manner that is easily absorbed by the reader. Representative microscopy images chosen do not always match the corresponding graphical summary and are not clear even on PDF version compared to (Lebeau J, et al. 2018 - full citation above).”

__Our Response to Reviewer #1 Comment #5. __We carefully edited the revised manuscript.We also confirmed that representative images match the observed quantifications.

Reviewer #1 Comment #6. “In order to further investigate the contribution PRELID1-dependent accumulation of PA in the OMM and its role in mitochondrial elongation, the authors should investigate the abundance of PA (and other lipids) in Perk, Prelid, Yme1l KO mutants. These experiments should quantitatively complement the results in Figure 5. KD of Prelid would be expected to increase mitochondrial elongation but there is no difference compared to WT in Figure 5.”

Our Response to Reviewer #1 Comment #6. __We thank the reviewer for this comment and now include new data to further demonstrate that co-treatment with the PERK kinase inhibitor GSK2656157 inhibits Tg-dependent increases in PA, while the PERK signaling inhibitor ISRIB does not (__Fig. 2B __and __Fig. S2A-E). Further, it is published that Perk-deletion inhibits ER stress-induced increases in PA, while knockin cells expressing the non-phosphorylatable eIF2a S51A mutant do not (Bobrovnikova-Marjon et al (2012) Mol Cell Biol). This is consistent with a model whereby PERK-dependent increases in PA are attributed to a PERK kinase-dependent, yet eIF2a phosphorylation-independent, mechanism. In the revised manuscript, we include additional quantification of PA across other genetic manipulations, as requested. Notably, we confirm that Lipin1 overexpression reduced basal PA and prevents Tg-dependent increases in PA (Fig. 2C, Fig. S2F,G). Further, we show that PRELID1 depletion does not significantly impact Tg-dependent increases of PA (Fig. S5B).

However, it is important to highlight that our work is specifically monitoring how acute ER stress-dependent PERK activation impacts mitochondria. Genetic manipulations that target many of the core components of these pathways are well established to globally disrupt many aspects of mitochondrial biology. Thus, these types of genetic manipulations often confound our ability to accurately monitor the contribution of specific stress-responsive signaling pathways in adapting mitochondria in response to acute insults. For example, a recent publication demonstrates that deletion of Perk impairs ER-mitochondrial phospholipid transport through mechanism independent of PERK kinase activity (Sassano et al (2023) J Cell Biol). While this problem can be limited if specific perturbations do not basally disrupt the phenotype being monitored (e.g., PRELID1 depletion does not significantly impact basal mitochondrial morphology; Fig. 5), our ability to evaluate how stress-responsive signaling regulates mitochondria in response to acute insults (e.g., ER stress) still requires temporal control to properly evaluate how these pathways impact aspects of mitochondrial biology. It is for this reason that we paired PRELID1 depletion with pharmacologic interventions that can be used to temporally inhibit PERK signaling (e.g., ISRIB, GSK), allowing us to best define the specific role for PERK-dependent reductions PRELID1 in promoting mitochondrial elongation in response to ER stress.

Reviewer #1 Comment #7. “Title of the subsection: "hypomorphic PERK variants inhibit ER..." is inappropriate since authors only investigated a single hypomorphic variant (PSP). KO mutant is a null not hypomorphic mutant”

__Our Response to Reviewer #1 Comment #7. __We agree and have made the suggested change in the revised manuscript.

Reviewer #1 Comment #8. “Can the authors elaborate on the possible biological relevance for the inhibition of OPA1 cleavage via Tg treatment?”

Our Response to Reviewer #1 Comment #8. __We show that Tg pretreatment inhibits mitochondrial depolarization induced by CCCP (__Fig. S3G). Thus, the impaired CCCP-induced, OMA1-dependent OPA1 processing observed in response to pretreatment with Tg likely reflects disruptions in mitochondrial uncoupling afforded by this treatment. We make this point clearer in the revised manuscript.

Line 170: “However, Tg pretreatment inhibited CCCP-induced proteolytic cleavage of the inner membrane GTPase OPA1 (Fig. 3C) – a biological process upstream of DRP1 in mitochondrial fragmentation induced by membrane uncoupling.43-47,64 This appears to result from Tg-dependent increases in mitochondrial membrane polarity (Fig. S3G), preventing efficient uncoupling in CCCP-treated cells and precluding our ability to determine whether Tg pretreatment directly impairs DRP1 activity under these conditions..”

Reviewer #1 Comment #9. “PRELID is a known short-lived protein; can the authors elaborate on possible additional impact due to 3-6 hr Tg treatment which is sufficient to induce expression of ATF4 target genes (Figure S2G).”

Our Response to Reviewer #1 Comment #9. PRELID1 is a short-lived mitochondrial protein that is rapidly degraded in response to acute ER insults. As demonstrated in Fig. 4 of our manuscript, this reduction is mediated by the IMM protease YME1L downstream of PERK-regulated translation attenuation. This 3-6 h timecourse corresponds with the translational attenuation induced downstream of PERK-dependent eIF2a phosphorylation following treatment with Tg and corresponds with the loss of PRELID1 observed in Tg-treated cells.

Note that the increase in ATF4 noted by the reviewer reflects the fact that ATF4 (and related proteins) are preferentially translated following eIF2a phosphorylation due to the presence of uORFs in their promoter. Thus, while global protein translation (including PRELID1 translation) is reduced by eIF2a phosphorylation, proteins like ATF4 are selectively translated.

Reviewer #1 Comment #10. “Thapsigargin induced ER stress does not only activate PERK arm of the ISR, correct? Could the authors comment on this?”

__Our Response to Reviewer #1 Comment #10. __I believe the reviewer is asking whether Tg treatment activates other arms of the integrated stress response (ISR). At the short timepoints used in this work (3-6 h), Tg-dependent increases in ISR signaling can be fully attributed to PERK signaling. This is evident as Perk deletion or inhibition blocks markers of ISR signaling in cells treated with Tg for these shorter timepoints (e.g., __Fig. 4E __of this paper; Harding et al (2002) Mol Cell and Lebeau et al (2018) Cell Reports). While other ISR kinases can be activated in response to more prolonged ER stress, the ISR activation observed in these shorter treatments with Tg are well established to be attributed to PERK activity.

Tg does induce all three arms of the unfolded protein response (i.e., ATF6, IRE1, and PERK) in the 3-6 h timeframe used in this manuscript. We previously showed that pharmacologic inhibition of ATF6 and IRE1 activity does not influence Tg-induced mitochondrial elongation (Lebeau et al (2018) Cell Reports). However, as reproduced in this manuscript, inhibition of PERK signaling blocks ER stress induced mitochondrial elongation. We make this point clearer in the revised manuscript.

Line 86. “Pharmacologic inhibition of PERK signaling, but not other arms of the UPR, blocks mitochondrial elongation induced by ER stress.39”

Reviewer #1 Comment #11. “*Addition of drugs and duration (3-6 hrs) likely very toxic to cells; how does this treatment affect viability? Unhealthy cells will have unhealthy mitochondria so it's hard to be confident that subtle morphological differences are specific. Why do authors use 3 hrs Tg-treatment after initially using 6 hrs in Figure 1? Would be helpful to assay toxicity and mitochondrial morphology of thapsigargin and other drugs in WT vs. Perk KO MEFs over time.” *

__Our Response to Reviewer #1 Comment #11. __Thapsigargin (Tg) is toxic to cells, but apoptosis is observed in cell culture models only after much longer treatments 24-72 h. We are using Tg to monitor how cells respond to acute ER stress. We chose the short 3-6 h timecourse because this is sufficient to induce PERK-dependent translation attenuation independent of cell death. Consistent with this, we observe no reductions in cellular viability or death in the short 3-6 h treatments used in this study. This timecourse is standard in the field when monitoring cellular changes induced by acute ER stress.

Reviewer #1 Comment #12. “Previously, an increase in fragmentation was observed at 0.5 hours but this subsided by 6 hours in WT (Lebeau J, et al. 2018) but is this the same for Perk KO MEFs?”

Our Response to Reviewer #1 Comment #12. __The increase in mitochondrial fragmentation observed following Tg treatment results from the rapid increase of mitochondrial Ca2+ induced by this treatment (Hom et al (2007) J Cell Phy). Consistent with this, we have found that pharmacologic inhibition of PERK signaling using the compound ISRIB, does not inhibit mitochondrial fragmentation in MEFmtGFP cells treated for 30 min with Tg. Since Perk-deficient MEFs already show increased fragmentation (__Fig. 1B,C), monitoring mitochondrial morphology in Perk-deficient cells treated with Tg for 30 min is unlikely to reveal additional insights into the mechanism outlined in this manuscript.

Reviewer #1 Comment #13. “How much protein was loaded per lane and what was the percentage of polyacrylamide gel? Please clarify details in methodology.”

Our Response to Reviewer #1 Comment #13. We loaded 100 µg of protein for our immunoblotting experiments. We used 10% or 12% SDS-PAGE gels. We included this information in the revised Materials and Methods.

Reviewer #1 Comment #14. “Figure 1A is virtually identical to Figure 2A (with exception of "MEF A/A") from previous publication: Lebeau J, Saunders JM, Moraes VWR, Madhavan A, Madrazo N, Anthony MC, Wiseman RL. The PERK Arm of the Unfolded Protein Response Regulates Mitochondrial Morphology during Acute Endoplasmic Reticulum Stress. Cell Rep. 2018 Mar 13;22(11):2827-2836. doi: 10.1016/j.celrep.2018.02.055. PMID: 29539413; PMCID: PMC5870888.”

Our Response to Reviewer #1 Comment #14. __Yes. __Fig. 1A is a cartoon showing PERK-dependent regulation of mitochondria and the specific pharmacologic and genetic manipulations used in this paper to alter this pathway. This is adapted from our previous manuscript (Lebeau et al (2018) Cell Reports). We properly reference this adaptation in the revised manuscript. We feel it is important to show this figure to specifically highlight how different manipulations influence this signaling pathway.

Reviewer #1 Comment #15. “If the authors' hypothesis is correct, overexpression of PRELID1 should have same effect as overexpression of Lipin”

Our Response to Reviewer #1 Comment #15. Overexpressed PRELID1 will be sensitive to the same rapid YME1L-dependent degradation observed for the endogenous protein. Thus, overexpressing PRELID1 would be expected to have no effect (or a very minor effect) on mitochondrial morphology in Tg-treated cells. We show that Lipin1 overexpression basally increases mitochondrial fragmentation and blocks Tg-induced mitochondrial elongation (Fig. 2). Identical results were observed in cells overexpressing the alternative PA lipase PA-PLA1 (Fig. S2). We feel that these data, in combination with others shown in our manuscript, strongly support the dependence of this process on PA levels and localization.

Reviewer #1 Comment #16. “What is the selective marker used for HeLa cells expressing mitoPLDGFP since the HeLa parental cell background already expressed a mitochondrial targeted GFP, we assume it was puromycin but this was not clear in the Figure legend or methods? If so, it would be helpful to clarify this. If not, how can the authors observe a difference in morphology if the selectable marker is the same? Indeed, mitoPLDGFP is expressed, detectable by immunoblot, but this is on a cell population level so no way of knowing whether the specific cells scored expressed mitoPLDGFP unless another selectable marker was used (i.e. should have used CFP, RFP, etc.).”

“The authors state "Note the expression of mitoPLDGFP did not impair our ability to accurately monitor mitochondrial morphology in these cells." in Figure 3 legend and again basically the same in S3: "Note that the expression of the mitoPLDGFP did not impair our ability to monitor mitochondrial morphology in these cells." Could the authors explain their reasoning here?”

__Our Response to Reviewer #1 Comment #16. __We co-transfected the mitochondrial localized mitoPLD-GFP with mtGFP in HeLa cells using calcium phosphate transfection. In using this approach, we (and others) have consistently found that this method leads to the efficient transfection of cells with both plasmids. Thus, cells will express both mitoPLD-GFP and mtGFP. We used mitoPLD-GFP because we were reproducing published experiments (Adachi et al (2016) Mol Cell) and we wanted to use the same overexpression plasmid used in these previous studies. It is clear from our images that the presence of GFP-tagged mitoPLD did not influence our ability to accurately monitor mitochondrial elongation in these cells. Further, the robust increase in mitochondrial elongation observed in cells overexpressing mitoPLD-GFP and the further increase in elongation observed upon co-treatment with Tg demonstrate the effectiveness of this assay. This is consistent with published results (Adachi et al (2016) Mol Cell).

Reviewer #1 Comment #17. ____“Figure S4C: the authors show that Tg treatment on MEF mtGFP cells for distinct hours to determine PRELID levels. However, in the Results section states that this treatment was with CHX, could the authors please check this and correct?”

Our Response to Reviewer #1 Comment #17. __The data shown in __Fig. S4C from the previous version is in Tg-treated cells. We corrected this in the revised manuscript.

Reviewer #1 Comment #18. “Figure 6: A schematic representation should be a graphic summary of all findings reported in the text with no text except where absolutely essential. A good model should be easily understood without reading any description since all concepts were supported in the main text and by experimentation.”

*“The model also contains some inaccuracies. The suggestion is that the authors re-do the model and clarify some aspects such as: *

*The model suggests that ISRIB inhibits PRELID1 directly but there is no evidence for this whereas PRELID is directly regulated by YME1L (also typo here in figure: "Yme1" no "l"). *

*This model incorrectly uses inhibition symbols; for example, mutation of Perk does not inhibit its activity as GSK does. The KO does not have Perk so cannot perform its function. These are not the same. *

Similarly, the lipases (Lipin and PA-PLA1) should be depicted instead as altering flux of PA away from OMM not as inhibition.

The authors should connect PA accumulation in the OMM graphically to mitochondrial elongation [instead of through text]. If the authors consider the numbered labels convenient, please use just the number and place the description in the figure legend instead.”

Our Response to Reviewer #1 Comment #18. __We have adapted our model shown in __Fig. 6 and the accompanying legend to address points brought up by the reviewer. In particular, because the reviewer found it difficult to follow how specific manipulations impacted specific steps, we removed those parts from the revised figure for clarity.

__Reviewer #1 Comment #19. __The reviewer made many suggestions to improve the Materials and Methods section of this manuscript in their review, which we do not include here for space considerations.

__Our Response to Reviewer #1 Comment #19. __We have addressed all of the reviewer’s comments regarding the Materials and Methods section in our revised manuscript.

Reviewer #1 Comment #20. The reviewer made many suggestions about the presentation of our figures that we do not include here for space considerations.

Our Response to Reviewer #1 Comment #20. __We have addressed all of the reviewer’s comments regarding the Figures__ in our revised manuscript.

REVIEWER #2.

Reviewer #2 General Comments. “Previous studies have shown that ER stress increases amounts of phosphatidic acid (PA) (PMID: 22493067) and induces elongation of mitochondria through the protein and lipid kinase PERK (PMID: 29539413, work by Wiseman's lab). The current work reports that ER stress by thapsigargin promotes the degradation of a mitochondrial protein PRELID1, which transfers PA from the outer membrane to the inner membrane. An inner membrane protease, YME1L, was identified as responsible for this degradation of PRELID1. Consistent with the notion that PA is required for the morphological change, overexpression of a PA phosphatase (Lipin) or a PA phospholipase (PA-PLA1) decreased ER-stress-induced mitochondrial elongation.”

“Overall, this manuscript is a nice extension of the authors' previous work and investigates the molecular mechanism underlying the regulation of mitochondrial elongation induced by ER stress. However, the current data do not strongly support the role of PRELID1 in either ER-stress-mediated PA level elevation or mitochondrial elongation, as described in Specific comments. The authors should address these points.”

__Our Response to Reviewer #2 General Comments. __We thank the reviewer for the thorough and careful read of our manuscript. We address the specific points brought up by the reviewer in our revised manuscript, as described below.

Reviewer #2 Comment #1. “The authors report that PRELID1 knockdown did not promote mitochondrial elongation under either normal or ER-stress conditions (Fig. 5). If PRELID1 plays a vital role in mitochondrial elongation, PRELID1 depletion will restore elongation. Therefore, the presented data argue against the authors' conclusion. Since PRELID1 has multiple homologs, including PRELID3B, which is also a short-lived protein like PRELID1, these homologs might redundantly function in PA transport, especially when PRELID1 is absent. Therefore, the authors need to knock them down simultaneously. This possibility is consistent with the previous authors' data that YME1L depletion decreases ER-stress-induced mitochondrial elongation (PMID: 29539413). YME1L knockdown may rescue multiple short-lived PRELID1 homologs.”

Our Response to Reviewer #2 Comment #1. __Our model indicates that ER stress-dependent increases in mitochondrial elongation require two steps: 1) PERK kinase-dependent increases in total PA and 2) YME1L-dependent degradation of PRELID1 downstream of PERK-dependent translation attenuation. Thus, it is not surprising that PRELID1 depletion did not induce mitochondrial elongation on its own. However, we do demonstrate that depletion of PRELID1 rescues Tg-induced mitochondrial elongation in cells co-treated with the PERK signaling inhibitor ISRIB – a compound that specifically blocks Tg-dependent PRELID1 degradation, but not PERK kinase dependent increases in total PA (__Fig. 6). This demonstrates that PRELID1 reductions are required, but not sufficient for promoting mitochondrial elongation. We make this point more clear in the revised manuscript.

Line 259: “Interestingly, Prelid1 depletion did not basally influence mitochondrial morphology or inhibit Tg-induced mitochondrial elongation (Fig. 5A,B and Fig. S5E). This indicates that reduction of PRELID1, on its own, is not sufficient to increase mitochondrial elongation, likely reflecting the importance of PERK kinase-dependent increases in PA in this process.53”

With respect to PRELID3B/SLMO2. This lipid transporter is primarily associated with trafficking phosphatidylserine (PS) from the outer to the inner mitochondrial membrane, where it is then converted to phosphatidylethanolamine (PE). As alluded to by the reviewer, we found that SLMO2, like PRELID1, is also a short-lived mitochondrial protein that is rapidly degraded by YME1L downstream of PERK-dependent translation attenuation. We have also found that Tg treatment disrupts mitochondrial PE levels through a PERK-dependent mechanism on a similar timescale to that observed for PA changes. However, shRNA depletion of SLMO2 in HeLa cells – a condition that mimics the reductions in SLMO2 observed during ER stress – increases basal mitochondrial fragmentation and inhibits Tg-induced mitochondrial elongation. Since chronic, genetic reductions in SLMO2 (which mirror the acute reduction in SLMO2 observed during ER stress) show opposite impacts on mitochondrial morphology to that observed upon Tg treatment, we interpreted this result to indicate that SLMO2 reductions are likely not involved in PERK-dependent regulation of mitochondrial elongation during acute ER stress. In contrast, depletion of PRELID1 is sufficient to rescue Tg-induced mitochondrial elongation in cells co-treated with ISRIB (Fig. 5A-D) – a compound that selectively blocks ER stress-dependent reductions in PRELID1. This implicates reductions in PRELID1 in this process. We are continuing to define the specific impact of PERK-dependent regulation of SLMO2 on mitochondrial morphology, ultrastructure, and/or function in work outside the scope of this current manuscript, but we felt it most appropriate to focus this manuscript on PA-dependent morphology remodeling based on the presented data.

Reviewer #2 Comment #2. “Another possibility is that since a previous study has shown that PERK-produced PA activates the mTOR-AKT pathway (PMID: 22493067), this signaling pathway may contribute to mitochondrial morphology in addition to PRELID1. The authors should test the combined effects of mTOR-AKT inhibition in ER-stress-induced mitochondrial elongation.”

Our Response to Reviewer #2 Comment #2. __As highlighted by the reviewer, PERK-dependent increases in PA can influence mTOR and AKT activity. To test this, we monitored mTOR-dependent S6K phosphorylation and AKT phosphorylation in MEFmtGFP and HeLa cells treated with Tg for 3 h. While we did observe increases in S6K phosphorylation in Tg-treated MEFmtGFP cells, mTOR activity was not changed in Tg-treated HeLa cells. AKT phosphorylation was not affected in MEFmtGFP or HeLa cells (not shown). We include these mTOR data in the revised manuscript (see __Fig. S3C,D). Since we observe PERK-dependent mitochondrial elongation in both MEFmtGFP and HeLa cells, we interpret these results to indicate that PA-dependent increases in mTOR activity is not primarily responsible for ER stress dependent increases in mitochondrial elongation across cell types. We describe these results in the revised manuscript.

Line 156: “In contrast, PERK-dependent increases in PA can activate mTOR during ER stress.53 Consistent with this, we observe Tg-dependent increases in mTOR-dependent S6K phosphorylation in MEFmtGFP cells (Fig. S3C). However, despite increasing PA and promoting mitochondrial elongation, Tg did not increase S6K phosphorylation in HeLa cells (Fig. S3D). These results suggest that PERK-dependent alterations in mTOR activity are unlikely to be primary contributors to ER stress induced mitochondrial elongation across cell types.”

Reviewer #2 Comment #3. “The authors' model suggests the loss of PRELID1 increases PA levels in the mitochondrial outer membrane (Fig. 6). The authors should test PA levels in mitochondria isolated from cells depleted for PRELID1 and its homologs (simultaneously). Since PA that is transported to the inner membrane is actively converted to other phospholipids, such as CDP-DAG, elevated levels of PA are likely seen if the outer membrane to inner membrane transport is blocked.

Our Response to Reviewer #2 Comment #3. __We agree with the reviewer it is important to evaluate how PERK-dependent degradation of PRELID1 impacts other phospholipids dependent on PA trafficking to the IM where it can be converted to other lipids, most notably cardiolipin (CL). In the revised manuscript, we now show measurements of CL in MEFmtGFP cells treated with Tg and/or depleted of Prelid1. As expected, reductions in PRELID1 decrease CL in isolated mitochondria (__Fig. S5C). Treatment with Tg reduced CL to similar extents in MEFmtGFP-treated cells expressing non-silencing shRNA. However, we did not observe further reductions of CL in Prelid1-depleted cells. This is consistent with a model whereby ER stress-dependent reductions in PRELID1 decrease PA trafficking across the IMS and lead to reductions in CL synthesis. These results are discussed in the revised manuscript as below:

Line 214. “PRELID1 traffics PA from the outer to inner mitochondrial membrane, where it serves as a precursor to the formation of cardiolipin.56,66,67* Thus, reductions in PRELID1 should decrease cardiolipin. To test this, we shRNA-depleted Prelid1 from MEFmGFP cells and monitored cardiolipin in isolated mitochondria in the presence or absence of ER stress. We confirmed efficient PRELID1 knockdown by immunoblotting (Fig. S5A). Importantly, Prelid1 depletion did not alter Tg-induced reductions of TIM17A or increases of ATF4. Further, Tg-dependent increases in PA were observed in Prelid1-depleted MEFmtGFP cells (Fig. S5B). These results indicate that loss of PRELID1 does not impair PERK signaling in these cells. Prelid1 depletion reduced cardiolipin in mitochondria isolated from MEFmtGFP cells (Fig. S5C). Treatment of MEFmtGFP cells expressing non-silencing shRNA with Tg for 3 h also reduced cardiolipin to levels similar to those observed in Prelid1-deficient cells. However, Tg did not further reduce cardiolipin in Prelid-depleted cells. These results are consistent with a model whereby ER stress-dependent reductions in PRELID1 limit PA trafficking across the inner mitochondrial membrane and contribute to reductions in cardiolipin during acute ER stress.” *

We are continuing to define how PERK signaling influences other mitochondrial phospholipids during conditions of ER stress in work outside the scope of this manuscript. Notably, we are continuing to evaluate how ER stress and PERK signaling influences aspects of cardiolipin synthesis in response to both acute and chronic ER stress. Further, as discussed above, we are determining how PERK-dependent reductions in PRELID3B/SLMO2 influence PS trafficking and subsequent PE synthesis at the IM and the implications of these changes on mitochondrial biology. Initial experiments indicate that PERK signaling reduces PE during ER stress, indicating that other phospholipids can be influenced by this pathway. However, we view this work as being outside the scope of the current manuscript focused specifically on defining the impact of PA remodeling on mitochondrial morphology.

Reviewer #2 Comment #4. “The authors need to test whether Lipin and PA-PLA1 overexpression decreased PA levels in mitochondria treated with thapsigargin. The current manuscript only shows the effect of Lipin and PA-PLA1 on PA levels in whole-cell lysate without ER stress (Fig. S2F).”

Our Response to Reviewer #2 Comment #4. __We agree. In the revised manuscript, we now show that Lipin overexpression blocks Tg-dependent increases in PA (__Fig. 2C). Identical experiments are also shown for Prelid1-depleted cells (Fig. S5B).

Reviewer #2 Comment #5. “The authors propose that PA inhibits DRP1 in mitochondrial division under ER stress. It has been shown that PA blocks DRP1 after recruitment to mitochondria (PMID: 27635761). Does thapsigargin induce mitochondrial accumulation of DRP1?”

Our Response to Reviewer #2 Comment #5. __The reviewer is correct that our results suggest that ER stress promotes mitochondrial elongation through a model involving PA-dependent inhibition of mitochondrial fission at the outer membrane. In the revised manuscript, we now show that Tg treatment does not significantly influence the recovery of DRP1 in mitochondrial fractions (__Fig. S3A). Further, we recapitulate results from previous publications showing that Tg does not significantly influence DRP1 phosphorylation at either S637 or S616 (Fig. S3B). This indicates that DRP1 localization and posttranslational modification does not appear affected by Tg treatment. However, we do show that Tg pretreatment inhibits DRP1-dependent mitochondrial fission induced by ionomycin (Fig. 3D,E). Combined with other results, our data are consistent with a model whereby PERK-dependent increases in PA and PRELID1 degradation leads to the accumulation of PA on the OM where it can inhibit DRP1 activity (Fig. 6). We make this point clearer in the revised manuscript.

Line 154: “However, as reported previously39, Tg did not influence DRP1 phosphorylation at either S637 or S616 (Fig. S3A) or alter the amount of DRP1 enriched in mitochondrial fractions from MEFmtGFP cells (Fig. S3B).”

REVIEWER #3.

Reviewer #3 General Comments. “The authors investigated signaling pathways and molecular mechanisms leading to mitochondrial dysfunction after ER stress. This study extends their previous publication (Lebeau et al., 2018) by providing evidence on how PERK regulates mitochondrial structure and function in response to ER stress. Some key findings are that PERK induces mitochondrial elongation by increasing and retaining phosphatidic acid (PA) in the outer mitochondrial membrane which is important for cell adaptation and survival. This process requires PERK-dependent translational attenuation through YME1L-PRELID dependent mechanism. This is a very strong study with compelling evidence.”

“This study adds to our current knowledge on how ER stress affects mitochondria adaptation and proteostasis, which may contribute to the pathogenesis and progression of numerous neurodegenerative diseases. Specifically, this study establishes a new role for PERK in mitochondrial adaptive remodeling focused on trafficking and accumulation of phospholipids. Identifying molecular markers like PERK and its involvement with PRELID, YME1L, and PA to regulate mitochondrial remodeling during ER stress is important to understand the effects of drug-targeting this ER stress-responsive factor.”

__Our Response to Reviewer #3 General Comments. __We thank the reviewer for the enthusiastic comments about our manuscript. We address the reviewers remaining concerns as outlined below.

Reviewer #3 Comment #1. “Only one minor point should be addressed: In Fig S2G & H, the authors indicate that "Lipin1 overexpression did not significantly influence increases of ATF4 protein". The blots show a decrease in ATF4 in Tg-treated HeLa cells. The same effect is observed in Fig. S3F showing reduction in ATF4, but the authors described it as the "overexpression of mitoPLD did not significantly impact other aspects of PERK signaling in Tg-treated cells". The quantification of the blots or indication that the blots were quantified should be clarified and noted (at least in the legend).”

Our Response to Reviewer #3 Comment #1. __We agree. We now include quantification of ATF4 in immunoblots from HeLA cells overexpressing lipin1 and treated with Tg (__Fig. S2J). As we suggested, these results confirm that Tg treatment does not significantly influence ATF4 expression in these cells. In addition, we now include additional data showing that lipin overexpression does not significantly reduce Tg-dependent expression of ISR target genes including Asns or Chop (Fig. S2I). This further supports other findings in the manuscript showing that different manipulations do not significantly impact ISR signaling (evident by ATF4 expression or TIM17A or PRELID1 degradation).

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Referee #3

Evidence, reproducibility and clarity

The authors investigated signaling pathways and molecular mechanisms leading to mitochondrial dysfunction after ER stress. This study extends their previous publication (Lebeau et al., 2018) by providing evidence on how PERK regulates mitochondrial structure and function in response to ER stress. Some key findings are that PERK induces mitochondrial elongation by increasing and retaining phosphatidic acid (PA) in the outer mitochondrial membrane which is important for cell adaptation and survival. This process requires PERK-dependent translational attenuation through YME1L-PRELID dependent mechanism.

This is a very strong study with compelling evidence. Only one minor point should be addressed: In Fig S2G & H, the authors indicate that "Lipin1 overexpression did not significantly influence increases of ATF4 protein". The blots show a decrease in ATF4 in Tg-treated HeLa cells. The same effect is observed in Fig. S3F showing reduction in ATF4, but the authors described it as the "overexpression of mitoPLD did not significantly impact other aspects of PERK signaling in Tg-treated cells". The quantification of the blots or indication that the blots were quantified should be clarified and noted (at least in the legend).

Significance

This study adds to our current knowledge on how ER stress affects mitochondria adaptation and proteostasis, which may contribute to the pathogenesis and progression of numerous neurodegenerative diseases. Specifically, this study establishes a new role for PERK in mitochondrial adaptive remodeling focused on trafficking and accumulation of phospholipids. Identifying molecular markers like PERK and its involvement with PRELID, YME1L, and PA to regulate mitochondrial remodeling during ER stress is important to understand the effects of drug-targeting this ER stress-responsive factor.

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Referee #2

Evidence, reproducibility and clarity

Summary

Previous studies have shown that ER stress increases amounts of phosphatidic acid (PA) (PMID: 22493067) and induces elongation of mitochondria through the protein and lipid kinase PERK (PMID: 29539413, work by Wiseman's lab). The current work reports that ER stress by thapsigargin promotes the degradation of a mitochondrial protein PRELID1, which transfers PA from the outer membrane to the inner membrane. An inner membrane protease, YME1L, was identified as responsible for this degradation of PRELID1. Consistent with the notion that PA is required for the morphological change, overexpression of a PA phosphatase (Lipin) or a PA phospholipase (PA-PLA1) decreased ER-stress-induced mitochondrial elongation.

Specific comments

1. The authors report that PRELID1 knockdown did not promote mitochondrial elongation under either normal or ER-stress conditions (Fig. 5). If PRELID1 plays a vital role in mitochondrial elongation, PRELID1 depletion will restore elongation. Therefore, the presented data argue against the authors' conclusion. Since PRELID1 has multiple homologs, including PRELID3B, which is also a short-lived protein like PRELID1, these homologs might redundantly function in PA transport, especially when PRELID1 is absent. Therefore, the authors need to knock them down simultaneously. This possibility is consistent with the previous authors' data that YME1L depletion decreases ER-stress-induced mitochondrial elongation (PMID: 29539413). YME1L knockdown may rescue multiple short-lived PRELID1 homologs.
2. Another possibility is that since a previous study has shown that PERK-produced PA activates the mTOR-AKT pathway (PMID: 22493067), this signaling pathway may contribute to mitochondrial morphology in addition to PRELID1. The authors should test the combined effects of mTOR-AKT inhibition in ER-stress-induced mitochondrial elongation.
3. The authors' model suggests the loss of PRELID1 increases PA levels in the mitochondrial outer membrane (Fig. 6). The authors should test PA levels in mitochondria isolated from cells depleted for PRELID1 and its homologs (simultaneously). Since PA that is transported to the inner membrane is actively converted to other phospholipids, such as CDP-DAG, elevated levels of PA are likely seen if the outer membrane to inner membrane transport is blocked.
4. The authors need to test whether Lipin and PA-PLA1 overexpression decreased PA levels in mitochondria treated with thapsigargin. The current manuscript only shows the effect of Lipin and PA-PLA1 on PA levels in whole-cell lysate without ER stress (Fig. S2F).
5. The authors propose that PA inhibits DRP1 in mitochondrial division under ER stress. It has been shown that PA blocks DRP1 after recruitment to mitochondria (PMID: 27635761). Does thapsigargin induce mitochondrial accumulation of DRP1?

Significance

Overall, this manuscript is a nice extension of the authors' previous work and investigates the molecular mechanism underlying the regulation of mitochondrial elongation induced by ER stress. However, the current data do not strongly support the role of PRELID1 in either ER-stress-mediated PA level elevation or mitochondrial elongation, as described in Specific comments. The authors should address these points.

Audience ER stress, mitochondrial dynamics, membrane lipids, proteases

My Expertise mitochondrial dynamics, lipid biology

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Referee #1

Evidence, reproducibility and clarity

Summary:

This study investigates changes in mitochondrial morphology in response to ER stress due to pharmacological inhibition or genetic dysfunction in vitro via two different cell models (MEFs and HeLa cells). The authors specifically implicate the PERK branch of the ER-stress induced pathway in this process based on the observation that mitochondria elongate in response to thapsigargin (Tg) treatment which is blocked by the pathway inhibitors GSK and ISRIB or by genetic ablation of Perk/PERK. Homozygous knockout cells lacking PERK exhibit a fragmented mitochondrial phenotype even in the absence of Tg, which is rescued by expression of the wildtype but not a hypomorphic allele (PERKPSP). One of the more interesting suppositions of this manuscript is that mitochondrial elongation is dependent on the abundance of phosphatidic acid (PA); treatment with Tg provokes an increase in mitochondrial PA, but PA does not accumulate in mitochondria from cells co-treated with GSK, an inhibitor of PERK. This correlation suggests that increased mitochondrial PA accumulation is PERK-dependent. In addition, predicted manipulation of PA levels achieved by a gain of function expression of the lipase Lipin diminished mitochondrial elongation in response to ER stress. Similar results were obtained by PA-PLA1 overexpression, a cytosolic lipase that converts PA into lysophosphatidic acid (LPA). To further describe the mechanistic link between ER stress and mitochondrial morphology, the authors found that PRELID1, which transports PA from the OMM to the intermembrane space, and TIM17A, a component of the protein translocation machinery, were stabilized by loss of PERK or YME1L [and possibly an effect of ATF4], regardless of ER stress via Tg treatment. The authors also report that Tg treatment prevents OPA1 cleavage in cells treated with CCCP, an uncoupler of the proton gradient, suggesting that the effect due to Tg treatment is not through ER stress but decreased mitochondrial fusion via mito-stress induced OPA1 cleavage. To address this, cells were treated with ionomycin which induces mitochondrial fragmentation independent of DRP1. The authors observed an increase in mitochondrial fragmentation in the presence of ionomycin. However, co-treatment with Tg prevented fragmentation, as did overexpression of mitoPLDGFP, which converts cardiolipin to PA on the OMM. These results support a model in which, under ER stress conditions, PERK activation leads to translational attenuation, which leads to a decrease in the steady state levels of PRELID1 via YME1L-dependent degradation and to the accumulation of PA on the OMM. Based on published work this PA accumulation is expected to inhibit the mitochondrial division dynamin, DRP1. The authors tested this by examining the dependence of mitochondrial elongation on PRELID1.

Major comments:

1. Are the key conclusions convincing? A considerable amount of work was performed by the authors in preparation of this manuscript and while we find the model exciting, there are several issues that need to be addressed in order for the model to be sufficiently supported.
   1. Image quality of mitochondria is sub par and the images do not always appear representative of/match the accompanying histograms. When using a single fluorescent marker (mito-GFP), the images should be in grey scale.
   2. Mitochondria in Perk-/- MEFs are highly fragmented, which is potentially inconsistent with previous work (Lebeau J, et al. 2018) performed by the same research group. Can the authors comments on this discrepancy? Also, do the authors interpret this fragmentation to mean that Perk is required to maintain mitochondrial elongation in the absence of exogenous ER stress (Tg)? If so, the authors should test whether expression of a dominant negative version of DRP1 rescues this fragmented morphology. This would be an additional critical test of the authors' model.
   3. The authors postulate that mitochondrial elongation in response to Perk activation is specifically outer membrane PA-dependent negative regulation of DRP1. However, PA is readily convertible to other phospholipids, notably CL and LPA, both of which positively regulate mitochondrial fusion. The authors do not measure abundance of other phospholipids, particularly LPA or CL in their targeted lipidomics experiments, only PC. The authors need to consider this alternate possibility.
   4. In Figure 5, the authors found very little difference in mitochondrial elongation following knockdown of Prelid1 (comparison between vehicle only conditions), which is potentially inconsistent with their model as decreased PRELID1 should lead to increased OMM PA [and subsequently mitochondrial fusion/elongation].
   5. The manuscript requires more careful editing - there were grammatical and punctuation errors.
2. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? In Figure 5, the authors found very little difference in mitochondrial elongation following knockdown of Prelid1 (comparison between vehicle only conditions), which is potentially inconsistent with their model as decreased PRELID1 should lead to increased OMM PA [and subsequently mitochondrial fusion/elongation]. Therefore, these findings do not adequately support the authors' main model.
3. 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.
   • a. In order to further investigate the contribution PRELID1-dependent accumulation of PA in the OMM and its role in mitochondrial elongation, the authors should investigate the abundance of PA (and other lipids) in Perk, Prelid, Yme1l KO mutants. These experiments should quantitatively complement the results in Figure 5. KD of Prelid would be expected to increase mitochondrial elongation but there is no difference compared to WT in Figure 5.
   • b. The main premise is that ER-stress activates PERK which in turn leads to increased abundance of PA at the OMM in a PRELID1-dependent manner. PA has been shown to inactivate DRP1, resulting in decreased fission (and mitochondrial elongation). The authors should test their model by expressing a dominant negative allele of DRP1 to see if it rescues the fragmented morphology of Perk KO mutant.
4. 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.
   • a. The authors have all the necessary cell line and methods in hand, so we consider these experiments to be doable.
5. Are the data and the methods presented in such a way that they can be reproduced?
   • a. Not all are described in a way that could be easily reproduced (see specific comments below).
6. Are the experiments adequately replicated and statistical analysis adequate?
   • a. The foundation of this paper is based on qualitative analysis of confocal fluorescence microscopy images, but the chosen images are often not of high quality so performing statistical analysis in these cases is misleading. Also, each imaging-based experiment was performed three times, but with only 20 cells for each replicate. Does this represent sufficient statistical power?

Specific major comments by section

Introduction - No additional major comments.

Results - Title of the subsection: "hypomorphic PERK variants inhibit ER..." is inappropriate since authors only investigated a single hypomorphic variant (PSP). KO mutant is a null not hypomorphic mutant.

Discussion - Can the authors elaborate on the possible biological relevance for the inhibition of OPA1 cleavage via Tg treatment? - PRELID is a known short-lived protein; can the authors elaborate on possible additional impact due to 3-6 hr Tg treatment which is sufficient to induce expression of ATF4 target genes (Figure S2G). - Thapsigargin induced ER stress does not only activate PERK arm of the ISR, correct? Could the authors comment on this?

Methods - Addition of drugs and duration (3-6 hrs) likely very toxic to cells; how does this treatment affect viability? Unhealthy cells will have unhealthy mitochondria so it's hard to be confident that subtle morphological differences are specific. Why do authors use 3 hrs Tg-treatment after initially using 6 hrs in Figure 1? Would be helpful to assay toxicity and mitochondrial morphology of thapsigargin and other drugs in WT vs. Perk KO MEFs over time. Previously, an increase in fragmentation was observed at 0.5 hours but this subsided by 6 hours in WT (Lebeau J, et al. 2018) but is this the same for Perk KO MEFs? Figures/supplementary figures - General: - In several images there is substantial background GFP signal resulting in images that are fuzzy on the high quality PDF (printout is unintelligible). - Example: Figure 2, Mock+veh. - Example: Figure S2I, Mock+veh, +PA-PLA Tg. - Example: Figure 3C mock+veh. - Mitochondrial morphology doesn't appear uniform even within the same cell so how is this accounted for in scoring of mitochondrial morphology? Also, how are authors scoring mitochondrial morphology? Due to the inconsistencies in the chosen images, we feel this manuscript would benefit from addition of a supplementary figure showing examples for each cell model expressing mtGFP (i.e. HeLa and MEFs) depicting the fragmented, tubular and elongated mitochondria. This should be able to be constructed from images already collected for these analyses that weren't already used in the paper. - Images from prior paper (Lebeau J, et al. 2018) are of much higher quality and is much easier to discern mitochondrial phenotype. - How much protein was loaded per lane and what was the percentage of polyacrylamide gel? Please clarify details in methodology. - Figure 1: - See general comments. - Figure 1A is virtually identical to Figure 2A (with exception of "MEF A/A") from previous publication: Lebeau J, Saunders JM, Moraes VWR, Madhavan A, Madrazo N, Anthony MC, Wiseman RL. The PERK Arm of the Unfolded Protein Response Regulates Mitochondrial Morphology during Acute Endoplasmic Reticulum Stress. Cell Rep. 2018 Mar 13;22(11):2827-2836. doi: 10.1016/j.celrep.2018.02.055. PMID: 29539413; PMCID: PMC5870888. - Figure 1B: the complemented Perk KO + vehicle should be similar to WT vehicle, but those images look quite different, even so, the respective bars are equal. - Vehicle treated Perk-/- cells have fragmented morphology which is different from Figure 2F in above publication by same group. Can the authors explain this discrepancy? - Figure S1: - No additional major comments. - Figure 2: - See general comments. - If the authors' hypothesis is correct, overexpression of PRELID1 should have same effect as overexpression of Lipin. ● Figure S2: - Images in Figure S2I are not representative of corresponding bars in Figure S2J (specifically vehicle treated panels). The "+PA-PLA1+Tg" panel instead appears fragmented (in comparison with other images). - Do authors have clearer images to substitute for CHX-treated panels? ● Figure 3: - What is the selective marker used for HeLa cells expressing mitoPLDGFP since the HeLa parental cell background already expressed a mitochondrial targeted GFP, we assume it was puromycin but this was not clear in the Figure legend or methods? If so, it would be helpful to clarify this. If not, how can the authors observe a difference in morphology if the selectable marker is the same? Indeed, mitoPLDGFP is expressed, detectable by immunoblot, but this is on a cell population level so no way of knowing whether the specific cells scored expressed mitoPLDGFP unless another selectable marker was used (i.e. should have used CFP, RFP, etc.). - The authors state "Note the expression of mitoPLDGFP did not impair our ability to accurately monitor mitochondrial morphology in these cells." in Figure 3 legend and again basically the same in S3: "Note that the expression of the mitoPLDGFP did not impair our ability to monitor mitochondrial morphology in these cells." Could the authors explain their reasoning here? - Figure S3: - Same as in Figure 3; "mock+Veh" appears more fragmented than tubular so is there a more representative image that the authors can show? - Figure 4: - No major comments. - Figure S4: - Figure S4C: the authors show that Tg treatment on MEF mtGFP cells for distinct hours to determine PRELID levels. However, in the Results section states that this treatment was with CHX, could the authors please check this and correct? - Figure 5: - 5C: PLKO NS shRNA +Tg appears more fragmented than tubular; do the authors have a more representative image? - Figure S5: - No major comments. - Figure 6: - A schematic representation should be a graphic summary of all findings reported in the text with no text except where absolutely essential. A good model should be easily understood without reading any description since all concepts were supported in the main text and by experimentation. - The model also contains some inaccuracies. The suggestion is that the authors re-do the model and clarify some aspects such as: - The model suggests that ISRIB inhibits PRELID1 directly but there is no evidence for this whereas PRELID is directly regulated by YME1L (also typo here in figure: "Yme1" no "l"). - This model incorrectly uses inhibition symbols; for example, mutation of Perk does not inhibit its activity as GSK does. The KO does not have Perk so cannot perform its function. These are not the same. Similarly, the lipases (Lipin and PA-PLA1) should be depicted instead as altering flux of PA away from OMM not as inhibition. - The authors should connect PA accumulation in the OMM graphically to mitochondrial elongation [instead of through text]. If the authors consider the numbered labels convenient, please use just the number and place the description in the figure legend instead.

Minor comments:

1. Specific experimental issues that are easily addressable.
   • a. Yes, please see specific examples below.
2. Are prior studies referenced appropriately?
   • a. References appeared adequate except in the Materials and Methods section (see specific examples below).
3. Are the text and figures clear and accurate?
   • a. No, the text needs considerable editing to make the language clearer and formal whereas the figures are not always presented in a manner that is easily absorbed by the reader. Representative microscopy images chosen do not always match the corresponding graphical summary and are not clear even on PDF version compared to (Lebeau J, et al. 2018 - full citation above).
4. Do you have suggestions that would help the authors improve the presentation of their data and conclusions?
   • a. Yes, please see specific examples below.

Specific minor comments by section

Introduction - This section contains minor grammatical errors and awkward writing which should be rephrased to be more concise. For example: - Incorrect use of commas (ex: absence of commas on page 3, bottom of paragraph 3).

Results - Overall, this section contains many grammatical errors and awkward language but these are unevenly distributed as some subsections are well written and thoroughly edited whereas others need closer inspection. For example: - No period at end of first subsection title; this should be consistent throughout. - Text not consistently written in past tense/passive voice. - Post-translational should be hyphenated (page 5, 2x on bottom of page). - The use of dashes to conjoin thoughts is too casual and sentences should be restructured with the aid of parentheses or semicolons only when necessary (ex: page 6, paragraph 2 through page 7). - Homogenize the use of hyphens in all sentences such as: ER stress-induced, ER stress-dependent.

Discussion

• Minor grammatical errors and awkward wording throughout; description of ideas should be more concisely written. For example:
  • Page 13, paragraph 1: "Thus, an improved understanding of how different PERK-dependent alterations to mitochondrial morphology and function integrate will provide additional insight to the critical importance of this pathway in regulating mitochondria during conditions of ER stress."
  • Page 13, paragraph 2: "Further investigations will be required to determine the specific impact of altered PERK signaling on mitochondria morphology and function in the context of these diseases to reveal both the pathologic and potentially therapeutic implications of PERK activity on the mitochondrial dysfunction observed in the pathogenesis of these disorders."
• Awkward/oxymoronic word choices. For example:
  • Page 11, paragraph 2: "...GSK2606414 reduces Tg-dependent increases of PA..." could be written as "... blocks/limits Tg-dependent increase of PA..." instead.
• What is evidence that ionomycin is completely independent of DRP1?

Methods

• Please provide more description or a reference for the method used for CRISPR/Cas9 gene editing (page 15, paragraph 1).
• Since different versions of chemicals are often available from the same company (for example in solution vs. powder, as a salt, different purities, etc.) it would be helpful for the authors to also include the catalog number for the purchased drugs and analytical standards (page 16, paragraph 1).
• The authors did an excellent job of blinding these images and utilizing several researchers to score each. However, we feel that 20 cells per biological replicate (~60 total per condition) is insufficient when mitochondrial morphology in chosen representative images is unclear. We think it is reasonable to request the authors to score additional images they collected as part of this investigation.
• The below two sentences contain some redundancies and should be combined/rephrased (page 16, paragraph 2).
  • "Three different researchers scored each set of images and these scores were averaged for each individual experiment. All quantifications shown were performed for at least 3 independent experiments, where averages in morphology quantified from each individual experiment were then combined."
• Incorrect units, for example: "500g" should be "500 x g" on page 16, paragraph 3 and "g" should be italicized. Same for "200g" on page 17, paragraph 1.
• Inconsistent abbreviation of chemicals, for example:
  • Chloroform and hydrochloric acid but not methanol in methods on page 17, paragraph 1. Also, the "l" in "HCL" should be lowercase.
• "Solvents" (2x) on page 17, paragraph 2 should be singular not plural.
• What does RT stand for on page 17, paragraph 2?
• Tris buffered saline is abbreviated incorrectly as "TB" then correctly later in the same paragraph as "TBS" on page 18, paragraph 3.
• Paragraph 4 on page 18 should be indented to be consistent with formatting of previous methods sections.
• To remove any ambiguity, catalog numbers should be included for antibodies (also consider including the lot number as there can be lot to lot variability).
• What percentage of tween v/v was supplemented in TBS buffer? Different concentrations of tween can impact antibody binding and would beneficial to include for reproducibility.
• Please indicate the incubation time and conditions for the secondary antibodies.
• The abbreviation for phosphate buffered saline is "PBS" not "PBD" (page 19, paragraph 1).
• Could the authors state clearly the reference transcript used for RT-qPCR (assumed is RIBOP)?
• Sometimes GIBCO is capitalized, sometimes not (Gibco), which should also be consistent.
• Who is the supplier for CCCP and what is the catalog number? Similarly, what is the catalog number for TMRE (both on page 19, paragraph 3)?
• Student's t-test is capitalized and possessive (similar to Tukey's) on page 19, paragraph 4.

Figures/supplementary figures

• General:
  • With respect to the lines overlaying histograms scoring mitochondrial morphology for designating statistical significance [with color-coded asterisks]:
    • It is assumed that the bars of the histogram being compared are those at the ends of each line but these aren't aligned perfectly. Please tidy up the figure by shifting these and consider capping lines to make more clear.
    • It appears that the authors provide these lines at all instances of statistically significant differences whether the comparison is important to their conclusions or not; including only the necessary comparisons will reduce the noise of these figures and make them easier to absorb and interpret. For example:
    • Figure 1C: why is comparison being made only for KO vs. complemented (+veh) - difference between KO and WT not statistically significant? Also, wouldn't the difference between WT and KO +Tg percent fragmented be statistically significant? The comparisons being made appear arbitrary or if not, was not clearly stated (same criticism for 2D, 3B, 3D, etc.).
  • The authors appear to use "transfection" and "transduction" interchangeably such that it is unclear whether expression of transgenes or shRNA is stably vs. transiently expressed. It would help if the authors could clarify their language here as well.
• Figure 1:
  • Figure 1A - PERK is membrane bound not soluble; should this not be represented in the model? Model colors are not easily distinguishable from each other on printout and should be upgraded.
  • Figure 1C - phenotypic scoring is not easy to interpret; perhaps authors could rearrange the figure such that each treatment is adjacent since that is the more interesting comparison? All cells in figure 1 are MEFs so delete "MEFs" below Perk+/+ and Perk -/-.
• Figure S1:
  • How much protein was loaded per lane and what percentage of polyacrylamide gel was used?
• Figure 2:
  • See general comments.
  • Figure 2A - extra letter/typo in "Fold Change."
  • Why do authors switch to HeLa cells after measuring PA content in MEFs?
• Figure S2:
  • Authors are now including ns for "not significant" and the p value where before they were not before. The intent for including the p-value in S2B appears to be because it suggests a trend towards statistical significance (actually a bit surprised it is not based on SEM error bars; authors should recheck their calculations) which is inappropriate. Either provide all the p-values, possibly as a separate table or none at all.
  • Now including double headed error bars for S2D-E which is inconsistent with rest of manuscript.
  • What is standard error for vehicle treated cells in 3B, 3D, and 3E? Given the above mistake it's reasonable to suspect that the error bars were omitted by accident.
• Figure 3:
  • Title should have hyphen for "stress-induced" and ionomycin shouldn't be capitalized.
  • Now using double headed error bars for 3B which is inconsistent with majority of other figures.
• Figure S3:
  • Title should have hyphen for "stress-induced" and ionomycin shouldn't be capitalized.
• Figure 4:
  • What is the purpose of including 4A? This depicts a concept which is not particularly difficult to grasp, was not experimentally shown in this manuscript, and is somewhat redundant with Figure 6. We recommend removing from Figure 4 and combining with Figure 6.
  • Since all cells used in Figure 4 were MEFs, the authors can remove "MEFs" from figure and just include genotype.
  • Figure 4C: typo in Yme1l - has two 1's.
• Figure S4:
  • See general comments.
• Figure 5:
  • Figure 5C: What does PLKO abbreviation stand for in the control line? pLKO.1 vector (see methods but not explained further).
• Figure S5:
  • Figure S5A-B: KD clearly worked but how efficient is unclear (quantitatively, i.e. 50, 90%, etc.?). The authors could perform serial dilutions of protein (i.e. 5, 10, 20 ug of the same samples for SDS-PAGE/immunoblot) or RT-qPCR. If knockdown is incomplete, this could explain the discrepancy in Figure 5 where depletion of Prelid should result in elongation [via OMM depletion of PA].
• Figure 6:
  • This is a more appropriate location for panel 4A.

Significance

1. Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.
   • a. Perturbances in PERK signaling evoke an alteration in mitochondrial morphology and have been extensively reported on, due to their clinical implications on neurodegenerative disorders such as Alzheimer's disease. The present work provides insight into the molecular basis for Stress Induced Mitochondrial Hyperfusion (SIMH) which can be triggered by ER stress. The authors find that this process occurs downstream of PERK and proceeds through accumulation of PA in the OMM by stabilization of Prelid, a mitochondrial resident protein that transports PA from the OMM to IMM for cardiolipin synthesis. The evidence of this work represents a substantial addition to the field of mitochondrial dynamics/SIMH and the Unfolded Protein Response.
2. Place the work in the context of the existing literature (provide references, where appropriate).
   • a. The novelty of this work is in the inclusion of PRELID1 downstream of PERK signaling pathway for transmission of ER stress to the mitochondria, a process that involves phosphatidic acid (PA). Some studies have addressed how phosphatidic acid is a modulator and a signal in mitochondrial physiology. The role of the lipids in mitochondrial dynamics represent an important and emerging field that needs to be explored in order to understand how metabolites control mitochondrial fusion/fission.

References

Yoshihiro Adachi, Kie Itoh, Tatsuya Yamada, Kara L. Cerveny, Takamichi L. Suzuki, Patrick Macdonald, Michael A. Frohman, Rajesh Ramachandran, Miho Iijima, Hiromi Sesaki. Coincident Phosphatidic Acid Interaction Restrains Drp1 in Mitochondrial Division. Molecular Cell. Volume 63, Issue 6. 2016. Pages 1034-1043. https://doi.org/10.1016/j.molcel.2016.08.013

Huang H, Gao Q, Peng X, Choi SY, Sarma K, Ren H, Morris AJ, Frohman MA. piRNA-associated germline nuage formation and spermatogenesis require MitoPLD profusogenic mitochondrial-surface lipid signaling. Dev Cell. 2011 Mar 15;20(3):376-87. https://doi.org/10.1016/j.devcel.2011.01.004 3. State what audience might be interested in and influenced by the reported findings. - a. Audiences of the fields such as Mitochondrial dynamics, UPR, lipid metabolism, neurodegenerative diseases, ER-stress response, Integrated Stress Response. 4. 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. - a. Mitochondrial morphology, mtDNA inheritance, mitochondrial metabolism, fluorescence/indirect immunofluorescence microscopy

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Reply to the reviewers

We thank all the reviewers for having raised constructive criticism to fortify the main message and improve the clarity of the manuscript. We appreciate that all reviewers found that our work addresses an important topic and is of interest to a broad audience. We believe that we have thoroughly addressed the concerns of the reviewers, especially with regard to 1) performing another SMC3 chromatin immunoprecipitation and sequencing (ChIP-seq) replicate and control, 2) including a later time point for the transcriptional data, and 3) performing additional characterization of the growth phenotype of the SMC3 conditional knockdown.

Reviewer #1

(Evidence, reproducibility and clarity (Required)):*

Summary The present work by Rosa et al., provides convincing data about the presence and functional relevance of the cohesin complex in Plasmodium falciparum blood stages. In accordance with other organisms, the composition of the cohesin complex containing SMC1, SMC3 RAD21 and putatively STAG could be confirmed via pulldown and mass spectrometry. Basic characterization of endogenous tagged SMC3 demonstrated the expression and nuclear localization during IDC, as well as the relatively stable accumulation at centromeric regions, consistent with the known cohesin function in chromatid separation. Furthermore, dynamic and stage-dependent binding to intergenic regions observed in ChIPseq and major transcriptome aberrations upon knockdown of SMC3 (__Response: __As we regularly perform ChIP-seq experiments in the lab, we have generated multiple negative control datasets. In our opinion, the most stringent negative control for an HA-tagged protein is performing ChIP with an HA antibody in a WT strain. We have recently published an in-depth analysis of this (and other) negative ChIP-seq controls (Baumgarten & Bryant, 2022, https://doi.org/10.12688/openreseurope.14836.2). We show in this publication that non-specific ChIP-seq experiments (such as negative controls) result in an over-representation of HP1-heterochromatinized regions due to differences in sonication efficiency of heterochromatin and technical challenges with mapping regions with high levels of homology. In the anti-HA in WT ChIP negative control (performed at 12hpi), we do not see any enrichment at centromeric regions, but rather at heterochromatinized regions where clonally variant gene families are located. We performed peak calling analysis and found no significant overlap between the negative control ChIP-seq and the SMC3-3HA ChIP-seq data at 12hpi.

In addition, we have now performed a second biological replicate of the SMC3-3HA ChIP-seq with a different clone at all time points. We compared this data to that from the original clone and found significant overlap of the peaks called (see what is now Table 4 and Supp. Fig. 3A). We generated a stringent list of peaks that were shared between both clones at each time point and repeated all downstream analyses (see what are now Tables 5-8). We found that our conclusions were largely unchanged. Text describing these experiments and analyses have been added throughout the results section.

• Proposed mechanism of repressive effect of SMC3 early in IDC on genes, that get de-repressed in late stages: To claim this mode of function, it would be necessary to include a KD on late stage parasites. If there is an early repressive role of SMC3, upregulated genes should not be affected by late SMC3-KD. __Response: __To be clear, we are most interested in the transcriptional role of SMC3 during interphase, where results are not confounded by its potential role in mitosis. However, we did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to the manuscript (see Tables 11-13). Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi (see what is now Supp. Fig. 5B). Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.

To address the question of whether genes that are upregulated upon depletion of SMC3 at early stages are affected at the 36hpi time point, we performed differential expression analysis of the SMC3-3HA-glmS parasites with and without glucosamine at 36hpi (we have added this data in Table 11). Again, significantly up- and down-regulated genes were not filtered using the WT dataset. With this analysis, we see only three genes from the list of invasion-related genes (Hu et al., 2010) that are up-regulated, but none of them have a significant q-value (Tab 5 of Table 18). Thus, depletion of SMC3 in late stage parasites does not lead to up-regulation of the same genes that are upregulated at 12 and 24hpi. We have added this information to the text (Line 273).

Furthermore, the hypothesized repressive effect of SMC3 does not explain the numerous genes downregulated in KD.

__Response: __As we state on line 350, we do not observe enrichment of SMC3 at downregulated genes, suggesting an indirect or secondary effect of SMC3 KD on these genes.

• Due to the fact, that the KD was induced at the exact same timepoint and analysed 12h and 24h after induction it is possible that identified, differentially expressed genes at 24h are not directly regulated by SMC3, but rather due to a general deregulation of gene expression. Did the authors attempt to analyse gene expression upon induction at ring, trophozoite and schizont stage? Response: __As we state on line 230, in order to achieve SMC3 KD at the protein level, we had to treat the parasite with glucosamine for two cell cycles (approximately 96 hours). After two cell cycles of glucosamine treatment, the parasites were tightly synchronized and sampled 12 and 24 hours later. Thus, SMC3 KD takes place over the course of multiple days, but parasites are collected after stringent synchronization. Giemsa staining and bioinformatic analysis (line 250) of the RNA-seq data from parasites (with or without glucosamine) harvested at 12 and 24 hpi show that these parasites were synchronous and that there were no gross differences in genome-wide transcript levels. It is certainly possible that differentially expressed genes at 12 or 24hpi are not directly regulated by SMC3, and this is precisely why we perform ChIP-seq of SMC3: to provide evidence of direct involvement via binding, as stated on line 281. __

• *Based on rapid parasite growth, the authors hypothesize a higher invasion rate due to upregulation of invasion genes. This hypothesis is not supported by quantitative invasion assays or quantification of invasion factors on the protein level. An alternative explanation could be a shorter cell cycle (__Response: __We have repeated the growth curve analysis with additional clones and no longer observe a growth phenotype in the SMC3 knockdown condition. We have added images of Giemsa-stained parasites from the knockdown time course we performed to what is now Supp. Fig. 5A. We see no obvious differences in cell morphology caused by glucosamine treatment in the WT or SMC3-3HA-glmS parasites.

• Correlation of SMC3-occupancy/ATAC/expression profile of the exemplary genes rap2 and gap45 (Figure 4C,D,E): is this representative for all upregulated genes? __Response: __SMC3 occupancy shown at rap2 and gap45 is representative for all upregulated genes (see Fig. 4A and B). It is difficult to provide a general representation of the average expression profiles of all up-regulated genes over the course of the IDC, but Fig. 3E shows that the vast majority of up-regulated genes normally reach their peak expression in late stage parasites. With regard to ATAC-seq profiles, we have performed a metagene analysis of chromatin accessibility (data taken from (Toenhake et al., 2018)) at all up-regulated genes at time points that closely correspond to the time points used in our study: 15, 25, and 35, and 40 hpi (new Fig. 4C). This metagene analysis confirms what we observe at individual genes: increasing chromatin accessibility over the course of the IDC at these genes’ promoters. While metagene analyses offer important information, we always try to show the raw data (as in new Figs. 4D-F) from individual examples as proof of principle.

• Given that SMC3 appears to be not essential for parasite growth, the authors could generate a null mutant for SMC3, which might allow for easier analysis of differences in gene regulation, cell cycle progression and/or invasion efficiency. __Response: __As we explain on line 327, very little cohesin is required for normal growth and/or mitosis in our study and two studies in S. cerevisiae and D. melanogaster. However, SMC3 is essential in S. cerevisiae. We were unable to knock out SMC3, and a recent mutagenesis study suggests that SMC3 and SMC1 are essential to the parasite during the intraerythrocytic developmental cycle (Zhang et al. Science, 2018). This is why we chose an inducible knockdown system.

*Reviewer #1 (Significance (Required)):

Own opinion The authors provide a basic characterization of the cohesin component SMC3 using NGS methods to investigate chromatin binding sites and its potential influence on gene expression. *

__Response: __We respectfully disagree that our study offers only a basic characterization of SMC3. We combine IFA, mass spectrometry, and both ChIP-seq and RNA-seq of SMC3 across the entire intraerythrocytic developmental cycle to provide the most detailed and comprehensive functional analysis of SMC3 in P. falciparum to date.

The localisation of SMC3 at centromers as described previously (Batugedara 2020) was confirmed. However, the dynamic binding to other regions in the genome, potentially mediated by other proteins, could not be resolved unequivocal with only one replicate of ChIPseq per time point.

__Response: __With regard to the replicates for ChIP-seq, please see our response to this same point above.

Similarly, the RNAseq data demonstrate the relevance of SMC3 for gene expression, but no clear picture of a regulatory mechanism can be drawn at his point. Lacking information about the mode of binding as well as the setup of transcriptome analysis (only two time-shifted sampling points after simultaneous glmS treatment for 96h resulting in incomplete knockdown) cannot definitely elucidate, if SMC3/cohesin is a chromatin factor that affects transcription of genes in general or a specific repressor of stage-specific genes. __Response: __We agree that we have not established a regulatory mechanism for how SMC3 achieves binding specificity. However, the combination of inducible knockdown (as SMC3 is essential to the cell cycle) and differential expression analysis with ChIP-seq from the same time points across the intraerythrocytic developmental cycle is the most stringent and standard approach in the field of epigenetics for determining the direct role of a chromatin-associated protein in gene expression. We provide a detailed explanation of how the transcriptome analysis was set up in the Results (lines 229-234) and Materials and Methods (lines 715-719) section. With regard to our sampling points being “time-shifted,” we provide bioinformatic analysis (line 246-251, what is now Supp. Fig. 5B) of the RNA-seq data from untreated and glucosamine-treated parasites showing highly similar “ages” with regard to progression through the intraerythrocytic developmental cycle. While we of course also monitor progression through the cell cycle with Giemsa staining (Supp. Fig. 5A), this bioinformatic analysis is the most stringent method of determining specific times in the cell cycle.

*The work will be interesting to a general audience, interested in gene regulation and chromatin remodelling

The reviewers are experts in Plasmodium cell biology and epigenetic regulation.*

Reviewer #2

(Evidence, reproducibility and clarity (Required)):

Rosa et al, Review Commons The manuscript by Rosa et al. addresses the function of the cohesion subunit Smc3 in gene regulation during the asexual life cycle of P. falciparum. Cohesin is a conserved protein complex involved in sister chromatin cohesion during mitosis and meiosis in eukaryotic cells. Cohesin also modulates transcription and DNA repair by mediating long range DNA interactions and regulating higher order chromatin structure in mammals and yeast. In P. falciparum, the Cohesin complex remains largely uncharacterized. In this manuscript, the authors present mass spectrometry data from co-IPs showing that Smc3 interacts with Smc1 and a putative Rad21 orthologue (Pf3D7_1440100, consistent with published data from Batugedara et al and Hilliers et al), as well as a putative STAG domain protein orthologue (PF3D7_1456500). Smc3 protein appears to be most abundant in schizonts, but ChIPseq indicates predominant enrichment of Smc3 in centromers in ring and trophozoite stages. In addition, Smc3 dynamically binds with low abundance to other loci across the genome; however, the enrichment is rather marginal and only a single replicate was conducted for each time point making the data interpretation difficult. Conditional knock-down using a GlmS ribozyme approach indicates that parasites with reduced levels of Smc3 have a mild growth advantage, which is only evident after five asexual replication cycles and which the authors attribute to the transcriptional upregulation of invasion-linked genes following Smc3 KD. Indeed, Smc3 seems to be more enriched upstream of genes that are upregulated after Smc3 KD in rings than in downregulated genes, indicating that Smc3/cohesin may have a function in supressing transcription of these schizont specific genes until they are needed. The manuscript is concise and very well written, however it suffers from the lack of experimental replicates for ChIP experiments and a better characterization of the phenotype of conditional KD parasites. * Major comments • In the mass spectrometry analysis, many seemingly irrelevant proteins are identified at similar abundance to the putative rad21 and ssc3 orthologues, and therefore the association with the cohesion complex seems to be based mostly on analogy to other species rather than statistical significance. Hence, it would be really nice to see a validation of the novel STAG domain and Rad21 proteins, for example by Co-IP using double transgenic parasites.*

__Response: __While our IP-MS data did not yield high numbers of peptides, the top most enriched proteins were SMC3 and SMC1. As we state on line 157, two previous studies have already shown a robust interaction between SMC1, SMC3, and RAD21 in Plasmodium, supporting the existence of a conserved cohesin complex. While the identification of the STAG domain-containing protein is interesting, the purpose of our IP-MS was less about redefining the cohesin complex in P. falciparum and more about confirming that the epitope-tagged SMC3 we generated was incorporated correctly into the cohesin complex and was specifically immunoprecipitated by the antibody we later use for western blot, immunofluorescence, and ChIP-seq analyses. However, to validate the results of ours and others’ mass spectrometry results, we generated two new parasite strains – SMC1-3HA-dd and STAG-3HA-dd – and an antibody against SMC3 (see what is now Supp. Fig. 1). We performed co-IP and western blot analysis with these strains and show an interaction between SMC1 and SMC3 and STAG and SMC3 (see what is now Supp. Fig. 2). This information has been added to the manuscript on lines 162-167.

• *The ChIPseq analysis presented here is based on single replicates for each of the three time points. The significance cutoffs for the peaks are rather high (q __Response: __In our experience, a significance cutoff of FDR As we regularly perform ChIP-seq experiments in the lab, we have generated multiple negative control datasets. In our opinion, the most stringent negative control for an HA-tagged protein is performing ChIP with an HA antibody in a WT strain. We have recently published an in-depth analysis of this (and other) negative ChIP-seq controls (Baumgarten & Bryant, 2022, https://doi.org/10.12688/openreseurope.14836.2). We show in this publication that non-specific ChIP-seq experiments (such as negative controls) result in an over-representation of HP1-heterochromatinized regions due to differences in sonication efficiency of heterochromatin and technical challenges with mapping regions with high levels of homology. In the anti-HA in WT ChIP negative control (performed at 12hpi), we do not see any enrichment at centromeric regions, but rather at heterochromatinized regions where clonally variant gene families are located. We performed peak calling analysis and found no significant overlap between the negative control ChIP-seq and the SMC3-3HA ChIP-seq data at 12hpi.

In addition, we have now performed a second biological replicate of the SMC3-3HA ChIP-seq with a different clone at all time points. We compared this data to that from the original clone and found significant overlap of the peaks called (see what is now Table 4 and Supp. Fig. 3A). We generated a stringent list of peaks that were shared between both clones at each time point and repeated all downstream analyses (see what are now Tables 5-8). We found that our conclusions were largely unchanged. Text describing these experiments and analyses have been added throughout the results section.

The SMC3 ChIP from Batugedara et al., 2020 was performed with an in-house generated antibody (not a commercially available, widely validated antibody as we use) at a single time point in the IDC: trophozoites. Batugedara et al. performed one replicate and did not have an input sample for normalization. Rather, it seems that they incubated beads, which were not bound by antibody or IgG, with their chromatin and used any sequenced reads from this beads sample to subtract from their SMC3 ChIP signal as means of normalization. According to ENCODE ChIP-seq standards, this is not a standard nor stringent way of performing ChIP-seq and the subsequent analysis. Because they did not generate a dataset for their ChIP input, it is not possible to call peaks as we do in our study and compare those peaks with ours.

• The authors argue that during schizogony, cohesin may no longer be required at centromers, explaining the low ChIPsignal at this stage (Line 301). However, during schizogony parasites undergo repeated rounds of DNA replication (S-phase) and mitosis (M-phase) to generate multinucleated parasites; and concentrated spots of Smc3 are observed in each nucleus in schizonts by IFA. In turn, the strong presence of Smc3 at centromers in ring stage parasites is surprising, particularly since the Western Blot in Figure 1D shows most expression of Smc3 in schizonts and least in rings; and Smc3 is undetectable in rings by IFA. Yet, the ChIP signal shows very strong enrichment at centromers, long before S phase produces sister chromatids. What could be the reason for this discrepancy? Again, ChIP replicates and controls would be helpful in distinguishing technical problems with the ChIP from biologically relevant differences. __Response: __We discuss in lines 337-342 not that cohesin is no longer required at centromeres during schizogony, but that its removal from centromeres may be required specifically for separation of sister chromatids, as is seen in other eukaryotes. We also discuss that the unique asynchronous mitosis in Plasmodium may lead to a mixed population of parasites at the time point sampled where there may be some centromeres with SMC3 present and some where it is absent to promote sister chromatid separation. Even though SMC3 may be evicted from centromeres to promote sister chromatid separation, it is likely re-loaded onto centromeres once this process is complete. This is most likely why we see foci of SMC3 in each nucleus of mature schizonts by IFA. With regard to the discrepancy between SMC3 levels in rings seen in total nuclear extracts (by western blot) and at centromeres (by ChIP-seq): the total level of a protein in the nucleus does not necessarily dictate the genome-wide binding pattern or the level of enrichment of that protein at specific loci in the genome. Moreover, if one molecule of SMC3 binds to each centromere, 14 molecules would be needed in a ring stage parasite while over 500 would be needed in a schizont (assuming that there are ~36 merozoites present). SMC3 binds to centromeres in interphase cells in other eukaryotes as well, and we speculate that this binding may play a role in the nuclear organization of centromeres, as we discuss starting on line 333.

• It is surprising that a conserved protein like Smc3 shows such a subtle phenotype, given that it is predicted to be essential and its orthologues have a function in mitosis. Generally, only limited data are presented to characterize the Smc3 KD parasites, and more detail should be included. For example validation of the parasite line using a PCR screen for integration and absence of wt, parasite morphology after KD, and/or analysis of the KD parasites for cell cycle status. __Response: __First, we have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B). As we discuss on line 342, very little intact cohesin complex seems to be required for normal growth and mitosis in S. cerevisiae and D. melanogaster, which is probably why we do not see an obvious growth or morphological phenotype. Because we could not generate SMC3 knockout parasites, there may be just enough SMC3 left to perform its vital function in our KD strain. We have added PCR data to demonstrate integration of the 3HA tag- and glmS ribozyme-encoding sequence in the clonal strains we are using for all experiments (see what is now Supp. Fig. 1A). Sanger sequencing was performed on these PCR products to confirm correct sequences. We also added images of Giemsa-stained parasites in untreated and glucosamine-treated parasites at all time points to demonstrate a lack of an obvious morphological phenotype in SMC3 KD parasites (see what is now Supp. Fig. 5A).

• Synchronization was performed at the beginning of the growth time course, which would be expected to result in a stepwise increase in parasitemia every 48 hours; however, the parasitemia according to Fig. 4F rises steadily, which would indicate that the parasites are actually not very synchronous. __Response: __We did indeed tightly synchronize these parasites and hope that the stepwise increase in parasitemia is seen better in our new growth curve analysis (see what is now Supp. Fig. 4B).

• The question of whether Smc3 causes a shorter parasite life cycle (quicker progression) or more invasion is important and could be experimentally addressed by purifying synchronous schizont stage parasites and determining their invasion rates as well as morphological examination of the Giemsa smears over the time course. __Response: __We have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B).

• Please also compare Smc3 transcriptional levels in transgenic parasites to those in wt parasites to rule out that the genetic modification has lead to artificial upregulation of Smc3 transcription. __Response: __We have added this data to what is now Supp. Fig. 4C, showing that there is no significant difference in SMC3 transcript levels between WT and SMC3-3HA-glmS strains. We have added this information to the text of the manuscript (Line 243). As we also generated an SMC3 antibody, we could demonstrate that there is no appreciable difference in SMC3 protein levels between WT and SMC3-3HA-glmS strains (see what is now Supp. Fig. 1D).

• According to Figure S2, even more genes were deregulated at the 12 hpi time point in the WT parasites than in Smc3 parasites, and even to a much higher extent. What "transcriptional age" did the WT control parasites have at each time point? __Response: __We have now included the transcriptional age of all strains, replicates, and treatments in what is now Supp. Fig. 5B. At the 12 hpi time point in particular, regardless of glucosamine treatment, the SMC3-3HA-glmS and WT parasites were highly synchronous. The only large discrepancy we see in transcriptional age is between untreated and glucosamine-treated WT parasites at 36 hpi, which is why we did not include this time point in our transcriptional analysis. We were also surprised by the number of genes that were de-regulated with simple glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.

• A negative correlation with transcription is well established in S. cerevisiae, particularly at inducible genes. How does Smc3 enrichment generally look like for genes that show maximal expression at each of the time point? __Response: __We have performed a metagene analysis of SMC3 enrichment at all genes at each respective time point, which we divided into quartiles of expression based on their FPKM values in the RNA-seq data from the corresponding time point in untreated SMC3-3HA-glmS parasites. This quartile analysis considers all genes, including genes that are not transcribed at all and regardless of whether a gene has a significant SMC3 peak or is differentially expressed upon SMC3 knockdown. At the 12 hpi time point, we do see an inverse correlation between SMC3 enrichment and gene transcription level, but this enrichment is most pronounced across genes bodies. We see the highest SMC3 enrichment at genes in the 4th (lowest) quartile category. For the other two time points, we do not see any obvious pattern of SMC3 enrichment with regard to transcriptional status.

• Line 590: according to the methods, a 36 hpi KD time point was also harvested. Why are the data not shown/analysed? __Response: __To be clear, we are most interested in the transcriptional role of SMC3 during interphase, where results are not confounded by its potential role in mitosis. However, we did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to the manuscript (see Tables 11-13). Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi (see what is now Supp. Fig. 5B). Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.

Minor Comments • Line 103/104: the hinge domain and ATPase head domain are mentioned, please annotate these in Figure 1A.

__Response: __We have annotated the hinge and ATPase domains.

• Figure 1D: the kDa scale is missing from the H3 WB. __Response: __We have added a kDa scale.

• What is the scale indicated by different colors in Fig. 2A? __Response: __The different colors (blue, coral, and green) only represent the 12, 24, and 36hpi time points, respectively. This color scheme is used throughout the manuscript. If the reviewer is referring to the color gradation within each circos plot, this does not indicate a specific scale. The maximum y-axis value for all circos plots is 24, as indicated in the figure legend.

• Line 189: it would also be interesting how many peaks are "conserved" between the different time points studied, so not only to compare the gene lists of closest genes but also the intersecting peaks and then the closest genes to the intersecting peaks. __Response: __We have added this information in Table 7 and in the manuscript starting on Line 203. Using the new dataset of consensus peaks between two replicates, there were 88 genes associated with an SMC3 peak across all three time points, most of which were close to a centromeric region.

• What is the distribution of the peaks over diverse genetic elements, such as gene bodies, introns, convergent/ divergent/ tandem intergenic regions? In yeast, cohesion is particularly enriched in convergent intergenic regions, so it would be interesting to see how this behaves in P. falciparum. __Response: __We would have liked to define how many peaks were in intergenic versus genic regions of the genome, but the dataset of “genes” from PlasmoDB includes UTRs. Thus, we would need a better annotation of the genome to perform this analysis. Regardless, we calculated the average SMC3 peak enrichment (shared between both replicates) in intergenic regions between convergent and divergent genes (see what is now Supp. Fig. 3B and Table 6). As we now state in the manuscript on line 198, we see a slight enrichment in regions between convergent genes at all time points, but the differences were not significant.

• Line 130 intra-chromosomal interactions (word missing) __Response: __Thank you for pointing this out. We have corrected this.

• Contrary to Figure 1D, the WB in Figure 3A indicates strong expression of Smc3 in rings. Please comment on this discrepancy. __Response: __While extracts from all time points were run on the same western blot in Fig. 1D and thus developed for the same amount of time, this was not the case for Fig. 3A. In Fig. 3A, the samples were run on different blots and exposed for different times, so while we can compare SMC3-HA levels between – and + glucosamine for each time point, the levels at 12 hpi cannot be quantitatively compared to those at 24 or 36hpi.

• What time point after glucosamine addition represents the WB in Fig. 3A? __Response: __The “12hpi” parasites were sampled approximately 108 hours post glucosamine addition and the “24hpi” parasites sampled approximately 120 hours post glucosamine addition. Basically, the parasites were treated with glucosamine for 96 hours, synchronized, and then harvested 12 and 24 hours later.

• Line 233 / Suppl Figure 3: Isn't it a bit concerning that the untreated control parasites at 24 hpi statistically corresponded to 18-19 hpi? And to what timepoint did the wt parasites correspond? __Response: __We are not concerned by this, and we have included the WT parasites in what is now Supp. Fig. 5B for better comparison. In the analysis presented in Supp. Fig. 5B, regardless of glucosamine presence or absence, the differences among replicates and strains at 12 and 24hpi are, in our opinion, minimal, amounting to one or two hours of the 48-hour IDC. In our extensive experience with RNA-seq across the P. falciparum lDC, this synchronization is extremely tight. As we describe on line 430 of the Materials and Methods, there is a ±3 hour window in our synchronization method, meaning that parasites harvested at 24hpi could be anywhere from 21-27hpi. In addition, the dataset that was used for comparison (from Bozdech et al., 2003) was generated in 2003 in a different laboratory using different strains with microarray. While comparing more recent RNA-seq data to this classic study has become well-established practice and is useful for comparing transcriptional age between replicates and strains, it is inevitable that the calculated “hpi” from (Bozdech et al., 2003) will differ somewhat from our experimental “hpi”. We have indeed seen this small discrepancy in predicted transcriptional age in several of our RNA-seq datasets (unrelated to this study) from trophozoites harvested at 24hpi.

• Line 264: "whether naturally or via knockdown" - the meaning of this sentence is not entirely clear __Response: __We are referring to depletion of SMC3 at promoters, either naturally (i.e. lack of binding at the promoter at 36hpi that is not the result of SMC3 knockdown, as we show in Fig. 4B) or via SMC3 knockdown, which is not natural but artificial.

• Figure 4 Legend: A, B, C etc. are mixed up. Response: Thank you for pointing this out. We have corrected this.

• Figure 4D: the differences seem to be marginally significant, even not significant at all (q=0.8) for gap45 at 12hpi. __Response: __If one defines a significance cutoff of q = 0.05 (as is common practice in differential expression analyses), then the differences are significant. For a small minority of invasion genes (such as gap45), we do observe significance at either 12 hpi or 24 hpi, but not both. Thus, we have removed the word “significant” from the descriptions of each dataset in Tab 1 of what is now Table 18. however, we do not believe that this rules out a role for SMC3 at such a gene during interphase. What is now Table 18 offers a longer list of invasion-related genes, most of which are more “significantly” affected than rap2 and gap45.

• Figure 4F shows FACS data using SYBR green as a DNA stain. The authors could exploit this data to look at the relative DNA content per cell as a measure of parasite stage, since more mature parasites will have more DNA (mean fluorescence intensity). How did the corresponding parasite cultures look in Giemsa smears? Response: We have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B). We have added images of Giemsa-stained parasites in untreated and glucosamine-treated parasites at all time points to demonstrate a lack of an obvious morphological phenotype in SMC3 KD parasites (see what is now Supp. Fig. 5A).

• Are RNAseq replicates biological replicates from independent experiments or technical replicates? __Response: __RNA-seq replicates are technical replicates from the same parasite clone.

• Why does the number of genes analysed for differential gene expression differ between the comparisons? __Response: __If the reviewer is referring to the discrepancy between the total number of genes for different time points [for example, between what is now Table 9 (12hpi) and Table 10 (24hpi)], this is because in the RNA-seq/differential expression analysis, there have to be reads mapping back to a gene in order for that gene to be included in the analysis. Thus, if a gene is not transcribed at a given time point in the treated or untreated samples, it will not be included in the analysis. Gene transcription fluctuates significantly over the course of the IDC, so different time points will have different total numbers of transcribed genes.

• Line 372: Do you mean the proteins or the genes? AP2-I has a peak at 24 hpi and 36 hpi, and its interacting AP2 factor Pf3D7_0613800 at all time points. __Response: __We are referring to the genes. With the new ChIP-seq analysis including the second replicate, there are no consensus SMC3 peaks associated with ap2-I, bdp1, or Pf3D7_0613800 (see what is now Table 7).

• Line 480: no aldolase was shown. __Response: __We have removed this sentence.

• Line 838: include GO analysis in methods __Response: __We have added this.

Reviewer #2 (Significance (Required)): The paper addresses the function of the cohesin complex in gene regulation of malaria parasites for the first time. Due to the conserved nature of the complex, the data may be interesting for a broad audience of scientists interested in nuclear biology and cell division/ gene regulation.

Reviewer #3

(Evidence, reproducibility and clarity (Required)):

*Summary:

In the presented manuscript by Rosa et al. the authors investigate the longstanding question of how P. falciparum achieves the tight transcriptional regulation of its genome despite the apparent absence of many canonical sequence specific transcription factor families found in other eukaryotes. To do this the authors investigate the role of the spatial organization of the genome in this context, by performing a functional characterization of the conserved cohesion subunit SMC3 and its putative role in transcriptional regulation in P. falciparum. Using Cas9 mediated genome editing the authors generated a SMC3-3xHA-glmS parasite line, which they subsequently used to show expression of the protein over the asexual replication cycle by western blot and IFA analysis. In addition, using co-IP experiments coupled with mass spectrometry they identified the additional components of the cohesion complex also found in other eukaryotes as interaction partners of SMC3 in the parasite, thereby confirming the presence of the conserved cohesin complex in P. falciparum. By using a combination of ChIP-seq and RNA-seq experiments in SMC3 knockdown parasites the authors furthermore show that a reduction of SMC3 resulted in the up-regulation of a specific set of genes involved in invasion and egress in the early stages of the asexual replication cycle and that this up-regulation in transcription is correlated with a loss of SMC3 enrichment at these genes. From these observations the authors conclude, that SMC3 binds dynamically to a subset of genes and works as a transcriptional repressor, ensuring the timely expression of the bound genes. Overall, the presented data is intriguing, of high quality and very well presented. However, there are some points, which should be addressed to bolster the conclusions drawn by the authors.

Major points: I was not able to find the deposited datasets in the BioProject database under the given accession number. This should obviously be addressed and would have been nice to be able to have a look at these datasets also for the review process. *__Response: __We apologize for not giving the reviewers access. As the manuscript has been made available as a pre-print (which includes data accession numbers), but has not yet been published, we have not activated access to the data on the database.

*SMC3-ChIP-seq experiments:

"168 were bound by SMC3 across all three time points (Fig. 2D). However, most SMC3-bound genes showed a dynamic binding pattern, with a peak present at only one or two time points (Fig. 2B,D)."

Here it would be interesting to actually have more than one replicate of each of these ChIP-seq time points. This could provide a better idea of how "dynamic" these binding patterns actually are. Furthermore, I was missing a list of these 168 genes, which are constantly bound by SMC3. Anything special about those? What actually happens to this subset of genes in the SMC3 knockdown parasites? Do they show similar transcriptional changes?*

__Response: __We have now performed a second biological replicate of the SMC3-3HA ChIP-seq with a different clone at all time points. We compared this data to that from the original clone and found significant overlap of the peaks called (see what is now Table 4 and Supp. Fig. 3A). We generated a stringent list of peaks that were shared between both clones at each time point and repeated all downstream analyses (see what are now Tables 5-8). We found that our conclusions were largely unchanged. Text describing these experiments and analyses have been added throughout the results section. Using the new dataset of consensus peaks between two replicates, there were 88 genes associated with an SMC3 peak across all three time points (see what is now Table 7). The genes that are associated with an SMC3 peak at all time points are, in general, those closest to centromeric/pericentromeric regions and show no obvious functional relationship to each other. Out of these 88 genes, four are significantly up- or downregulated at 12 hpi and 26 are significantly up- or downregulated at 24 hpi. The most significantly downregulated of these genes in both datasets is smc3 itself.

*SMC3-knockdown experiments:

In Sup. Fig. 1 there is a double band in the HA-western blot in the 2nd cycle -GlcN. sample. This second band is absent in all other HA-western shown. Have the authors any idea where that second band comes from?*

__Response: __As the reviewer says, we do not see this second band in most of our western blots. It is possible that it is just a small amount of degradation in the lysate.

In Figure 3A, the WB data shown is slightly contrasting the RNA-seq quantification (3B). The knock-down on protein level seems to be stronger in the 12 hpi samples here than in the 24 hpi samples. Although the band for HA-SMC3 is stronger at the 12 hpi TP there's no band visible in the + GlcN. sample. There's however in the 24 hpi samples. Could the authors comment on this?

Response: __With regard to the discrepancy of the knockdown and protein versus RNA level, it is quite common for transcript levels to not agree with protein levels. This is why we always confirm a transcriptional knockdown with western blot analysis using appropriate loading controls. We are not sure why there is a more dramatic knockdown of SMC3 at 12hpi than at 24hpi, as these samples came from the same culture, but were simply harvested 12 hours apart. __

*"Comparison of our RNA-seq data to the time course transcriptomics data from (Painter et al., 2018) revealed that SMC3 depletion at 12 hpi caused downregulation of genes that normally reach their peak expression in the trophozoite stage (18-30 hpi), with the majority of upregulated genes normally reaching their peak expression in the schizont and very early ring stages (40-2 hpi) (Fig. 3E). At 24 hpi, a similar trend is observed, with most downregulated genes normally peaking in expression in trophozoite stage (24-32 hpi) and the majority of upregulated genes peaking in expression at very early ring stage (2 hpi) (Fig. 3F)."

I'm not fully convinced by these presented results/conclusions. This dataset would greatly benefit from the inclusion of additional later time points.*

__Response: __To be clear, we are most interested in the transcriptional role of SMC3 during interphase, where results are not confounded by its potential role in mitosis. However, we did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to the manuscript (see Tables 11-13). Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi (see what is now Supp. Fig. 5B). Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.

We performed differential expression analysis of the SMC3-3HA-glmS parasites with and without glucosamine at 36hpi (we have added this data in Table 11). Again, significantly up- and down-regulated genes were not filtered using the WT dataset. With this analysis, we see only three genes from the list of invasion-related genes (Hu et al., 2010) that are up-regulated, but none of them have a significant q-value (Tab 5 of Table 18). Thus, depletion of SMC3 in late stage parasites does not lead to up-regulation of the same genes that are upregulated at 12 and 24hpi. We have added this information to the text (Line 277).

*The presented upregulation of the egress and invasion related genes is hard to pinpoint to be a direct effect of transcriptional changes due to the SMC3 knockdown. While there's a slight upregulation of these genes they still seem to be regulated in their normal overall transcriptional program as shown in Figure 4D/E. *

__Response: __We provide evidence of a direct effect of SMC3 binding by combining differential expression analysis performed upon SMC3 knockdown with SMC3 ChIP-seq at corresponding time points. As we show in what is now Fig. 4C and D, promoter accessibility of these egress/invasion genes correlates with their transcriptional activity. However, SMC3 binding to the promoters of these same genes shows inverse correlation with their transcriptional activity (what is now Fig. 4B and D). While we believe that SMC3 does contribute to the repression of these genes at specific time points during the cell cycle, it is highly likely that SMC3 is just one protein of many that regulates these genes. Moreover, and especially since we do not see a growth phenotype in the SMC3 KD, it is possible that another protein or even SMC1 could compensate for loss of SMC3 at these promoter regions. We now state these possibilities on lines 346 383 of the Discussion.

*So the changes could in theory also be explained by the differences in cell cycle progression which are present between +/- GlcN. cultures (Sup. Fig. 3). The presented normalization to the microarray data is a well-established practice to correct for this but, as presented seems to have its limitation with these parasite lines (line 233, glucosamine treated parasites harvested at 24 hpi correspond statistically to approximately 18-19 hpi (Supp. Fig. 3).) *

__Response: __In the analysis presented in what is now Supp. Fig. 5B, regardless of glucosamine presence or absence, the differences among replicates and strains at 12 and 24hpi are, in our opinion, minimal, amounting to one or two hours of the 48-hour IDC. In our extensive experience with RNA-seq across the P. falciparum lDC, this synchronization is extremely tight. As we describe on lines 416-421 of the Materials and Methods, there is a ±3 hour window in our synchronization method, meaning that parasites harvested at 24hpi could be anywhere from 21-27hpi. In addition, the dataset that was used for comparison (from Bozdech et al., 2003) was generated in 2003 in a different laboratory using different strains with microarray. While comparing more recent RNA-seq data to this classic study has become well-established practice and is useful for comparing transcriptional age between replicates and strains, it is inevitable that the calculated “hpi” from (Bozdech et al., 2003) will differ somewhat from our experimental “hpi”. We have indeed seen this small discrepancy in predicted transcriptional age in several of our RNA-seq datasets from trophozoites harvested at 24hpi.

By including additional later time points, one could actually follow the expression profiles over the whole cycle and elucidate if there's an actual transcriptional up-regulation of the genes, or if the + GlcN. parasites show a faster cell cycle progression, with a shifted peak expression timing compared to the - GlcN. parasites. __Response: __We did collect a 36hpi time point in the SMC3-3HA-glmS and WT strain, with and without glucosamine. We have added this last time point and the WT data from the other two time points to what is now Supp. Fig. 5. Unfortunately, and for reasons unknown, the WT replicates treated with glucosamine showed a significantly advanced “transcriptional age” compared to the other replicates at 36hpi. Thus, we did not feel comfortable performing the RNA-seq analysis as we did with the other two time points (i.e. subtracting up- and down-regulated genes from the WT control from the SMC3-3HA-glmS data sets). We have added this information to the results section (Lines 256 and 261). As the WT parasites treated with glucosamine were approximately 8 hours in advance of the untreated WT parasites for the 36hpi time point, any up- and down-regulated genes might have been due to differences in the cell cycle rather than due to glucosamine treatment. The glmS system of inducible knockdown is widely used in P. falciparum; however, to our knowledge, no lab has investigated whether glucosamine treatment affects transcription in wildtype cells over the course of the IDC. Thus, for accurate phenotypic characterization of any protein with this system with regard to transcriptomics, we thought it was important to provide an RNA-seq dataset to define the cohort of genes affected by glucosamine treatment in WT parasites. We hope that our study will demonstrate the importance of using stringent controls when using inducible knockdown systems.

*"These genes show SMC3 enrichment at their promoter regions at 12 and 24 hpi, but not at 36 hpi (Fig. 4C), and depletion of SMC3 resulted in upregulation at both 12 and 24 hpi (Fig. 4D). Comparison of the SMC3 ChIP-seq data with published Assay for Transposase-Accessible Chromatin using sequencing (ATAC-seq) data (Toenhake et al., 2018) and mRNA dynamics data (Painter et al., 2018) from similar time points in the IDC revealed that SMC3 binding at the promoter regions of these genes inversely correlates with chromatin accessibility (Fig. 4C) and their mRNA levels (Fig. 4E), which both peak in schizont stages. These data are consistent with a role of SMC3 in repressing this gene subset until their appropriate time of expression in the IDC."

The presented correlations certainly make an intriguing point towards the authors conclusion that SMC3/cohesin depletion from the promoter regions of the genes results in a de-repression of these genes and their transcriptional activation. However, the SMC3 knockdown is not complete and only up to 69% as presented on RNA level in these parasites. Therefore a control experiment which needs to be done is to actually show the loss of SMC3 from the presented activated example genes in the knockdown parasites. This could easily be done by ChIP-qPCR or even ChIP-seq, to get a global picture of the actual changes in SMC3 occupation in the knockdown parasites in correlation with changes in transcript levels. *__Response: __While SMC3-3HA-glmS knockdown is not complete at the RNA level, it is fairly robust at the protein level, especially at 12hpi (Fig. 3A).

*"These data suggest that SMC3 knockdown results in a faster progression through the cell cycle or a higher rate of egress/invasion."

The authors could greatly strengthen their conclusions by investigating this thoroughly. Pinpointing the observed phenotype to an actual increase in invasion or egress would add to the authors main conclusion that the loss of SMC3 de-regulates the timing of gene expression for these invasion related genes thereby increasing their transcript levels and thus leading to a higher rate of egress/invasion. To determine cell cycle progression simple comparisons between DNA content using a flow cytometer at timepoints together with visual inspection of Giemsa stained blood smears would give a ggod indication towards changes in cell cycle progression. In addition invasion/egress assays by counting newly invaded rings per schizont could reveal, if there are changes in the rate of egress/invasion upon SMC3 knockdown.*

Response: __We have repeated our growth curve analysis several times and with more clones and have concluded that there is not a significant growth phenotype in SMC3 KD parasites (see what is now Supp. Fig. 4B). We have added images of Giemsa-stained parasites from the knockdown time course we performed to what is now Supp. Fig. 5A. We see no obvious differences in cell morphology caused by glucosamine treatment in the WT or SMC3-3HA-glmS parasites. As we discuss on line 327, very little intact cohesin complex seems to be required for normal growth and mitosis in S. cerevisiae and D. melanogaster, which is probably why we do not see an obvious growth or morphological phenotype. We believe that SMC3 is probably only a part of a complex controlling transcription of these invasion or egress genes. Thus, the up-regulation of these genes upon SMC3 KD might not be enough to lead to a significant growth or invasion phenotype. __

*Minor points:

In the MM section on the Cas9 experiments it says dCas9 where it should be Cas9 (line 425)*

__Response: __Thank you for pointing this out. We have corrected this.

It would be great to add which HP1 antibody was used in which dilution in the IFAs to the MM section. __Response: __We have added this information to the Materials and Methods section.

In Figure 4C for the gap45 gene there's is some green peak floating around which should not be there. __Response: __Thank you for pointing this out, we have corrected it.

*Reviewer #3 (Significance (Required)):

Significance: The manuscript investigates a very timely topic by trying to uncover new molecular mechanisms of transcriptional regulation in P. falciparum. Investigating the role of the cohesin complex/SMC3 in this context provides valuable new insights to the field. While the first part with the description of the SMC3 cell line and the co-IP experiments largely confirms published data on the existence and composition of the cohesin complex in Plasmodium and its enrichment at the centromeres, the second part is especially intriguing since it investigates the molecular function of SMC3 in more detail. The results pointing to a role of SMC3/cohesin as a transcriptional repressor are of great interest to the field and will open up new concepts for future investigation.*

*Audience: The work is particularly interesting for people interested in gene regulatory processes in Plasmodium and Apicomplexan parasites in general. At the same time it also nicely points towards shared principles of gene regulation to other eukaryotes in relation to the spatial organization of the genome making the work also very interesting for a broader audience with interest in the general principles of gene regulatory processes in eukaryotic organisms.

Expertise: P. falciparum epignetics and chromatin biology / gene regulation / Cas9 gene editing*

CROSS-CONSULTATION COMMENTS

All reviewers agree that the paper addresses an important topic and provides convincing evidence for enrichment of the cohesin component Smc3 at P. falciparum centromers. In contrast, evidence for a function of Smc3 as a transcriptional repressor of genes in the first part of the parasite life cycle is less well supported. All reviewers agree that the statistical significance of the ChIP experiments needs to be impoved by including biological replicates. In addition, the phenotype of the conditional knock-down should be analysed in more detail by clarifying whether faster cell cycle progression or higher invasion rate are responsible for the observed growth adavantage. Inclusion of transcriptional data from a later time point in addition to the presented data for 12 hpi and 24 hpi was also requested by all reviewers. Finally, several inconsistencies require clarification.

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

In the presented manuscript by Rosa et al. the authors investigate the longstanding question of how P. falciparum achieves the tight transcriptional regulation of its genome despite the apparent absence of many canonical sequence specific transcription factor families found in other eukaryotes. To do this the authors investigate the role of the spatial organization of the genome in this context, by performing a functional characterization of the conserved cohesion subunit SMC3 and its putative role in transcriptional regulation in P. falciparum.

Using Cas9 mediated genome editing the authors generated a SMC3-3xHA-glmS parasite line, which they subsequently used to show expression of the protein over the asexual replication cycle by western blot and IFA analysis. In addition, using co-IP experiments coupled with mass spectrometry they identified the additional components of the cohesion complex also found in other eukaryotes as interaction partners of SMC3 in the parasite, thereby confirming the presence of the conserved cohesin complex in P. falciparum. By using a combination of ChIP-seq and RNA-seq experiments in SMC3 knockdown parasites the authors furthermore show that a reduction of SMC3 resulted in the up-regulation of a specific set of genes involved in invasion and egress in the early stages of the asexual replication cycle and that this up-regulation in transcription is correlated with a loss of SMC3 enrichment at these genes. From these observations the authors conclude, that SMC3 binds dynamically to a subset of genes and works as a transcriptional repressor, ensuring the timely expression of the bound genes.

Overall, the presented data is intriguing, of high quality and very well presented. However, there are some points, which should be addressed to bolster the conclusions drawn by the authors.

Major points:

I was not able to find the deposited datasets in the BioProject database under the given accession number. This should obviously be addressed and would have been nice to be able to have a look at these datasets also for the review process.

SMC3-ChIP-seq experiments:

"168 were bound by SMC3 across all three time points (Fig. 2D). However, most SMC3-bound genes showed a dynamic binding pattern, with a peak present at only one or two time points (Fig. 2B,D)."

Here it would be interesting to actually have more than one replicate of each of these ChIP-seq time points. This could provide a better idea of how "dynamic" these binding patterns actually are. Furthermore, I was missing a list of these 168 genes, which are constantly bound by SMC3. Anything special about those? What actually happens to this subset of genes in the SMC3 knockdown parasites? Do they show similar transcriptional changes?

SMC3-knockdown experiments:

In Sup. Fig. 1 there is a double band in the HA-western blot in the 2nd cycle -GlcN. sample. This second band is absent in all other HA-western shown. Have the authors any idea where that second band comes from?

In Figure 3A, the WB data shown is slightly contrasting the RNA-seq quantification (3B). The knock-down on protein level seems to be stronger in the 12 hpi samples here than in the 24 hpi samples. Although the band for HA-SMC3 is stronger at the 12 hpi TP there's no band visible in the + GlcN. sample. There's however in the 24 hpi samples. Could the authors comment on this?

"Comparison of our RNA-seq data to the time course transcriptomics data from (Painter et al., 2018) revealed that SMC3 depletion at 12 hpi caused downregulation of genes that normally reach their peak expression in the trophozoite stage (18-30 hpi), with the majority of upregulated genes normally reaching their peak expression in the schizont and very early ring stages (40-2 hpi) (Fig. 3E). At 24 hpi, a similar trend is observed, with most downregulated genes normally peaking in expression in trophozoite stage (24-32 hpi) and the majority of upregulated genes peaking in expression at very early ring stage (2 hpi) (Fig. 3F)."

I'm not fully convinced by these presented results/conclusions. This dataset would greatly benefit from the inclusion of additional later time points. The presented upregulation of the egress and invasion related genes is hard to pinpoint to be a direct effect of transcriptional changes due to the SMC3 knockdown. While there's a slight upregulation of these genes they still seem to be regulated in their normal overall transcriptional program as shown in Figure 4D/E. So the changes could in theory also be explained by the differences in cell cycle progression which are present between +/- GlcN. cultures (Sup. Fig. 3). The presented normalization to the microarray data is a well-established practice to correct for this but, as presented seems to have its limitation with these parasite lines (line 233, glucosamine treated parasites harvested at 24 hpi correspond statistically to approximately 18-19 hpi (Supp. Fig. 3).) By including additional later time points, one could actually follow the expression profiles over the whole cycle and elucidate if there's an actual transcriptional up-regulation of the genes, or if the + GlcN. parasites show a faster cell cycle progression, with a shifted peak expression timing compared to the - GlcN. parasites.

"These genes show SMC3 enrichment at their promoter regions at 12 and 24 hpi, but not at 36 hpi (Fig. 4C), and depletion of SMC3 resulted in upregulation at both 12 and 24 hpi (Fig. 4D). Comparison of the SMC3 ChIP-seq data with published Assay for Transposase-Accessible Chromatin using sequencing (ATAC-seq) data (Toenhake et al., 2018) and mRNA dynamics data (Painter et al., 2018) from similar time points in the IDC revealed that SMC3 binding at the promoter regions of these genes inversely correlates with chromatin accessibility (Fig. 4C) and their mRNA levels (Fig. 4E), which both peak in schizont stages. These data are consistent with a role of SMC3 in repressing this gene subset until their appropriate time of expression in the IDC."

The presented correlations certainly make an intriguing point towards the authors conclusion that SMC3/cohesin depletion from the promoter regions of the genes results in a de-repression of these genes and their transcriptional activation. However, the SMC3 knockdown is not complete and only up to 69% as presented on RNA level in these parasites. Therefore a control experiment which needs to be done is to actually show the loss of SMC3 from the presented activated example genes in the knockdown parasites. This could easily be done by ChIP-qPCR or even ChIP-seq, to get a global picture of the actual changes in SMC3 occupation in the knockdown parasites in correlation with changes in transcript levels.

"These data suggest that SMC3 knockdown results in a faster progression through the cell cycle or a higher rate of egress/invasion."

The authors could greatly strengthen their conclusions by investigating this thoroughly. Pinpointing the observed phenotype to an actual increase in invasion or egress would add to the authors main conclusion that the loss of SMC3 de-regulates the timing of gene expression for these invasion related genes thereby increasing their transcript levels and thus leading to a higher rate of egress/invasion. To determine cell cycle progression simple comparisons between DNA content using a flow cytometer at timepoints together with visual inspection of Giemsa stained blood smears would give a ggod indication towards changes in cell cycle progression. In addition invasion/egress assays by counting newly invaded rings per schizont could reveal, if there are changes in the rate of egress/invasion upon SMC3 knockdown.

Minor points:

In the MM section on the Cas9 experiments it says dCas9 where it should be Cas9 (line 425)

It would be great to add which HP1 antibody was used in which dilution in the IFAs to the MM section.

In Figure 4C for the gap45 gene there's is some green peak floating around which should not be there.

Significance

The manuscript investigates a very timely topic by trying to uncover new molecular mechanisms of transcriptional regulation in P. falciparum. Investigating the role of the cohesin complex/SMC3 in this context provides valuable new insights to the field. While the first part with the description of the SMC3 cell line and the co-IP experiments largely confirms published data on the existence and composition of the cohesin complex in Plasmodium and its enrichment at the centromeres, the second part is especially intriguing since it investigates the molecular function of SMC3 in more detail. The results pointing to a role of SMC3/cohesin as a transcriptional repressor are of great interest to the field and will open up new concepts for future investigation.

Audience:

The work is particularly interesting for people interested in gene regulatory processes in Plasmodium and Apicomplexan parasites in general. At the same time it also nicely points towards shared principles of gene regulation to other eukaryotes in relation to the spatial organization of the genome making the work also very interesting for a broader audience with interest in the general principles of gene regulatory processes in eukaryotic organisms.

Expertise:

P. falciparum epignetics and chromatin biology / gene regulation / Cas9 gene editing

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

Rosa et al, Review Commons

The manuscript by Rosa et al. addresses the function of the cohesion subunit Smc3 in gene regulation during the asexual life cycle of P. falciparum. Cohesin is a conserved protein complex involved in sister chromatin cohesion during mitosis and meiosis in eukaryotic cells. Cohesin also modulates transcription and DNA repair by mediating long range DNA interactions and regulating higher order chromatin structure in mammals and yeast. In P. falciparum, the Cohesin complex remains largely uncharacterized. In this manuscript, the authors present mass spectrometry data from co-IPs showing that Smc3 interacts with Smc1 and a putative Rad21 orthologue (Pf3D7_1440100, consistent with published data from Batugedara et al and Hilliers et al), as well as a putative STAG domain protein orthologue (PF3D7_1456500). Smc3 protein appears to be most abundant in schizonts, but ChIPseq indicates predominant enrichment of Smc3 in centromers in ring and trophozoite stages. In addition, Smc3 dynamically binds with low abundance to other loci across the genome; however, the enrichment is rather marginal and only a single replicate was conducted for each time point making the data interpretation difficult. Conditional knock-down using a GlmS ribozyme approach indicates that parasites with reduced levels of Smc3 have a mild growth advantage, which is only evident after five asexual replication cycles and which the authors attribute to the transcriptional upregulation of invasion-linked genes following Smc3 KD. Indeed, Smc3 seems to be more enriched upstream of genes that are upregulated after Smc3 KD in rings than in downregulated genes, indicating that Smc3/cohesin may have a function in supressing transcription of these schizont specific genes until they are needed. The manuscript is concise and very well written, however it suffers from the lack of experimental replicates for ChIP experiments and a better characterization of the phenotype of conditional KD parasites.

Major comments

• In the mass spectrometry analysis, many seemingly irrelevant proteins are identified at similar abundance to the putative rad21 and ssc3 orthologues, and therefore the association with the cohesion complex seems to be based mostly on analogy to other species rather than statistical significance. Hence, it would be really nice to see a validation of the novel STAG domain and Rad21 proteins, for example by Co-IP using double transgenic parasites.
• The ChIPseq analysis presented here is based on single replicates for each of the three time points. The significance cutoffs for the peaks are rather high (q < 0.05). Therefore, the relevance of the marginally enriched dynamic peaks (average relative enrichment of <1.2 fold for genes upregulated in rings 12 hpi in Figure 4A and B) does not appear to be very robust. Even in ChIPseq experiments using non-immune IgG, hundreds of peaks are usually called with MACS2 with a similar magnitude. So, to substantiate the data for extra-centromeric peaks convincingly, replicates and more stringent statistics are necessary. In addition, the authors should also compare their data to published PfSmc3 ChIP data from Batugedara et al 2020 (GSE116219).
• The authors argue that during schizogony, cohesin may no longer be required at centromers, explaining the low ChIPsignal at this stage (Line 301). However, during schizogony parasites undergo repeated rounds of DNA replication (S-phase) and mitosis (M-phase) to generate multinucleated parasites; and concentrated spots of Smc3 are observed in each nucleus in schizonts by IFA. In turn, the strong presence of Smc3 at centromers in ring stage parasites is surprising, particularly since the Western Blot in Figure 1D shows most expression of Smc3 in schizonts and least in rings; and Smc3 is undetectable in rings by IFA. Yet, the ChIP signal shows very strong enrichment at centromers, long before S phase produces sister chromatids. What could be the reason for this discrepancy? Again, ChIP replicates and controls would be helpful in distinguishing technical problems with the ChIP from biologically relevant differences.
• It is surprising that a conserved protein like Smc3 shows such a subtle phenotype, given that it is predicted to be essential and its orthologues have a function in mitosis. Generally, only limited data are presented to characterize the Smc3 KD parasites, and more detail should be included. For example validation of the parasite line using a PCR screen for integration and absence of wt, parasite morphology after KD, and/or analysis of the KD parasites for cell cycle status.
• Synchronization was performed at the beginning of the growth time course, which would be expected to result in a stepwise increase in parasitemia every 48 hours; however, the parasitemia according to Fig. 4F rises steadily, which would indicate that the parasites are actually not very synchronous.
• The question of whether Smc3 causes a shorter parasite life cycle (quicker progression) or more invasion is important and could be experimentally addressed by purifying synchronous schizont stage parasites and determining their invasion rates as well as morphological examination of the Giemsa smears over the time course.
• Please also compare Smc3 transcriptional levels in transgenic parasites to those in wt parasites to rule out that the genetic modification has lead to artificial upregulation of Smc3 transcription.
• According to Figure S2, even more genes were deregulated at the 12 hpi time point in the WT parasites than in Smc3 parasites, and even to a much higher extent. What "transcriptional age" did the WT control parasites have at each time point?
• A negative correlation with transcription is well established in S. cerevisiae, particularly at inducible genes. How does Smc3 enrichment generally look like for genes that show maximal expression at each of the time point?
• Line 590: according to the methods, a 36 hpi KD time point was also harvested. Why are the data not shown/analysed?

Minor Comments

• Line 103/104: the hinge domain and ATPase head domain are mentioned, please annotate these in Figure 1A.
• Figure 1D: the kDa scale is missing from the H3 WB.
• What is the scale indicated by different colors in Fig. 2A?
• Line 189: it would also be interesting how many peaks are "conserved" between the different time points studied, so not only to compare the gene lists of closest genes but also the intersecting peaks and then the closest genes to the intersecting peaks.
• What is the distribution of the peaks over diverse genetic elements, such as gene bodies, introns, convergent/ divergent/ tandem intergenic regions? In yeast, cohesion is particularly enriched in convergent intergenic regions, so it would be interesting to see how this behaves in P. falciparum.
• Line 130 intra-chromosomal interactions (word missing)
• Contrary to Figure 1D, the WB in Figure 3A indicates strong expression of Smc3 in rings. Please comment on this discrepancy.
• What time point after glucosamine addition represents the WB in Fig. 3A?
• Line 233 / Suppl Figure 3: Isn't it a bit concerning that the untreated control parasites at 24 hpi statistically corresponded to 18-19 hpi? And to what timepoint did the wt parasites correspond?
• Line 264: "whether naturally or via knockdown" - the meaning of this sentence is not entirely clear
• Figure 4 Legend: A, B, C etc. are mixed up.
• Figure 4D: the differences seem to be marginally significant, even not significant at all (q=0.8) for gap45 at 12hpi.
• Figure 4F shows FACS data using SYBR green as a DNA stain. The authors could exploit this data to look at the relative DNA content per cell as a measure of parasite stage, since more mature parasites will have more DNA (mean fluorescence intensity). How did the corresponding parasite cultures look in Giemsa smears?
• Are RNAseq replicates biological replicates from independent experiments or technical replicates?
• Why does the number of genes analysed for differential gene expression differ between the comparisons?
• Line 372: Do you mean the proteins or the genes? AP2-I has a peak at 24 hpi and 36 hpi, and its interacting AP2 factor Pf3D7_0613800 at all time points.
• Line 480: no aldolase was shown.
• Line 838: include GO analysis in methods

Referees cross-commenting

All reviewers agree that the paper addresses an important topic and provides convincing evidence for enrichment of the cohesin component Smc3 at P. falciparum centromers. In contrast, evidence for a function of Smc3 as a transcriptional repressor of genes in the first part of the parasite life cycle is less well supported. All reviewers agree that the statistical significance of the ChIP experiments needs to be impoved by including biological replicates. In addition, the phenotype of the conditional knock-down should be analysed in more detail by clarifying whether faster cell cycle progression or higher invasion rate are responsible for the observed growth adavantage. Inclusion of transcriptional data from a later time point in addition to the presented data for 12 hpi and 24 hpi was also requested by all reviewers. Finally, several inconsistencies require clarification.

Significance

The paper addresses the function of the cohesin complex in gene regulation of malaria parasites for the first time. Due to the conserved nature of the complex, the data may be interesting for a broad audience of scientists interested in nuclear biology and cell division/ gene regulation.

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Referee #1

Evidence, reproducibility and clarity

Summary

The present work by Rosa et al., provides convincing data about the presence and functional relevance of the cohesin complex in Plasmodium falciparum blood stages. In accordance with other organisms, the composition of the cohesin complex containing SMC1, SMC3 RAD21 and putatively STAG could be confirmed via pulldown and mass spectrometry. Basic characterization of endogenous tagged SMC3 demonstrated the expression and nuclear localization during IDC, as well as the relatively stable accumulation at centromeric regions, consistent with the known cohesin function in chromatid separation. Furthermore, dynamic and stage-dependent binding to intergenic regions observed in ChIPseq and major transcriptome aberrations upon knockdown of SMC3 (<70% mRNA reduction via glmS-system) suggest an important function in transcriptional regulation. The underlying mechanism of gene regulation by cohesin via the creation of chromatin clusters or DNA loops as well as its specificity to target sites remain speculation.

Major criticism

• Accuracy of ChIPseq with only one replicate per time point (and lacking negative controls without antibody) is not convincing. The authors should include more replicates.
• Proposed mechanism of repressive effect of SMC3 early in IDC on genes, that get de-repressed in late stages: To claim this mode of function, it would be necessary to include a KD on late stage parasites. If there is an early repressive role of SMC3, upregulated genes should not be affected by late SMC3-KD. Furthermore, the hypothesized repressive effect of SMC3 does not explain the numerous genes downregulated in KD.
• Due to the fact, that the KD was induced at the exact same timepoint and analysed 12h and 24h after induction it is possible that identified, differentially expressed genes at 24h are not directly regulated by SMC3, but rather due to a general deregulation of gene expression. Did the authors attempt to analyse gene expression upon induction at ring, trophozoite and schizont stage?
• Based on rapid parasite growth, the authors hypothesize a higher invasion rate due to upregulation of invasion genes. This hypothesis is not supported by quantitative invasion assays or quantification of invasion factors on the protein level. An alternative explanation could be a shorter cell cycle (<48h), as the different cell cycle progression estimation of KD/WT could indicate (SuppFigure 3). Giemsa-stain images of KD/WT parasites should be included to show normal stage development over time.
• Correlation of SMC3-occupancy/ATAC/expression profile of the exemplary genes rap2 and gap45 (Figure 4C,D,E): is this representative for all upregulated genes?
• Given that SMC3 appears to be not essential for parasite growth, the authors could generate a null mutant for SMC3, which might allow for easier analysis of differences in gene regulation, cell cycle progression and/or invasion efficiency.

Significance

Own opinion

The authors provide a basic characterization of the cohesin component SMC3 using NGS methods to investigate chromatin binding sites and its potential influence on gene expression. The localisation of SMC3 at centromers as described previously (Batugedara 2020) was confirmed. However, the dynamic binding to other regions in the genome, potentially mediated by other proteins, could not be resolved unequivocal with only one replicate of ChIPseq per time point. Similarly, the RNAseq data demonstrate the relevance of SMC3 for gene expression, but no clear picture of a regulatory mechanism can be drawn at his point. Lacking information about the mode of binding as well as the setup of transcriptome analysis (only two time-shifted sampling points after simultaneous glmS treatment for 96h resulting in incomplete knockdown) cannot definitely elucidate, if SMC3/cohesin is a chromatin factor that affects transcription of genes in general or a specific repressor of stage-specific genes.

The work will be interesting to a general audience, interested in gene regulation and chromatin remodelling

The reviewers are experts in Plasmodium cell biology and epigenetic regulation.

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Reply to the reviewers

The authors do not wish to provide a response at this time. The full point-by-point reply is attached together with the manuscript files.

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Referee #3

Evidence, reproducibility and clarity

Review Commons recommends including the following components in referee reports:

1. Evidence, reproducibility and clarity

Summary:

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

The manuscript by Awoniyi et al is an elegant study that addresses the protein composition of the lipid rafts upon BCR activation. The authors use an elegant system, employing the enzyme ascorbate peroxidase (APEX2), which in cellulo generates short-lived biotin radicals, that in turn randomly bind to proteins in their vicinity (10-20 nm) within 1 min. APEX2 is furthermore fused with the 7-amino acid sequence MGCVCSS, which allows its targeting to lipid rafts (Raft-APEX2) and with an mCherry marker. Using modern microscopy methods as well as quantitative mass-spectrometry proteomics, the authors provide a spatially and temporally resolved dynamic insight into the changes within the lipid raft and. are able to enrich multiple proteins in the lipid rafts previously not associated with BCR signaling. Furthermore, they identify Golga3 and Vti1b as proteins proximally responding to BCR activation possibly enabling vesicle transport.

The manuscript is generally well written, the study is well-conceived and well-controlled. Nevertheless, the authors may answer some important questions (see below)

Major comments:

• Are the key conclusions convincing?

Yes, the key conclusions of the study are convincing and based on elegant experiments

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

• 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.

• In Figure 2, the HEL-specific A20 B cells are stimulated with anti-IgM F(ab)'2. While, beyond a doubt, anti-IgM F(ab)'2 is a potent stimulus, which triggers BCR signaling activation, I am curious why the authors chose it over the HEL antigen.

• Describing figures 4 and 5, the authors state that they did not identify prominent BCR signaling pathway regulators. My major concern here is that the authors employ cancerous B cells for their analyses. The lipid raft composition and proteins recruited to the rafts in these cells may vary from those in primary wild-type B cells. While the authors do keep in mind that the signaling protein composition may vary between cell lines, it may vary even more between lymphoma B cell line and primary wild-type cells. Therefore, it may be beneficial to verify the expression of the "unexpected" proteins, such as Golga3, Kif20a, and Vtib1b in primary cells using immunofluorescence analyses similar to the ones presented in Fig 6.

• The authors mention in the discussion, that Syk was not identified in their data set. This is surprising as Syk has been attributed with an important role in the proximal BCR signaling (Kulathu et al, https://doi.org/10.1111/j.1600-065X.2009.00837.x)

• Would it be possible to detect Syk using the immunofluorescence technique from Figure 6?

• Additionally, as stated in the text, A20 cells express endogenous IgG2a. Have the authors tried to conduct similar experiments stimulating with anti-IgG antibodies instead of anti-IgM F(ab)'2?

• Have the authors tried to co-express the IgD-BCR to mimic mature peripheral B cells?

• 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.

I cannot estimate the cost but if conducted, some experiments might take several months

• 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?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

• Are prior studies referenced appropriately?

Yes

• Are the text and figures clear and accurate?

Yes, but, if possible, please provide the data instead of writing "data not shown"

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Fig. 1D and Supp. Fig. S1C: the authors state that after IgM cross-linking, the non-transfected and Raft-APEX2-transfected cells showed "indistinguishable" p-Tyr levels. From my perspective, the Raft-APEX2-transfected cells show higher levels of p-Tyr. It is possible to quantify it?

Some paragraph titles are very short and descriptive (e.g. Proteomic analysis, membrane-proximal proteome etc.). It could improve the reading if the paragraph titles consisted of respective key findings

Significance

2. Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

• This study dissects in a spatio-temporal manner the early events upon BCR stimulation and the enrichment of various proteins in the vicinity of lipid rafts. While conceptually not novel, the study provides novel methodology to address this question. This is technically relevant and worth to be published after a major revision.

• Place the work in the context of the existing literature (provide references, where appropriate).

*This study prominently overlooks a bulk of literature that supports the BCR dissociation activation model and does not comment that (reviewed in Maity et al, Volume 1853, Issue 4, April 2015, Pages 830-840)

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

The findings of this manuscript are specifically interesting for researchers who study early events of B cells activation, specifically the changes in the membrane composition and early BCR signaling

• 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.

Immunology, Molecular and Cell Biology

Referee Cross-commenting

I agree totally that "the article would greatly benefit from a follow-up investigation on the functional/physiological relevance of the proposed players", however only if this is easily done with the CRISP mediated knock out as mentioned by both reviewers. In addition it s interesting to see data on cells stimulated with the antigen instead of anti IgM fab'2.

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Referee #2

Evidence, reproducibility and clarity

Summary

Awoniyi et al. utilizes APEX2-mediated proximity proteomics to investigate the protein composition of lipid rafts and their dynamics in the context of B cell receptor (BCR) signaling. The authors add a 7 amino acid guide sequence to an APEX2-mCherry construct to specifically target the fusion protein into lipid raft plasma membrane domains and thereby spatially label and identify contained proteins. While a larger number of lipid raft-related proteins were verified, the study focuses on a smaller subset that is proposed to be specifically related to BCR signaling. Unexpectedly, this approach suggests key players of BCR signaling to be excluded from lipid rafts in an inducible manner. Finally, two of the identified proteins, Golga3 and Vti1b, were further investigated by immunofluorescence microscopy. Since both proteins are shown to be recruited to the plasma membrane and to colocalize with antigen, the authors propose Golga3 and Vti1b as novel targets of BCR activation and drivers of subsequent antigen internalization.

Major Comments

• A major claim of this study is that the majority of BCR signaling proteins (including CD79a and CD79b as parts of the BCR as well as BLNK) get excluded from lipid rafts upon stimulation. Moreover, many components of the endocytosis/vesicle trafficking pathways have been identified and the authors raise interesting points regarding the BCR as signaling platform versus the BCR as antigen internalization complex. This is intriguing and could even be explored further (e.g. by presenting Figure S3 in the main manuscript). However, the claim that Vti1b and Golga3 (and possibly Kif20) play key roles in the endocytic processes underlying BCR/antigen endocytosis and subsequent processing needs further verification e.g. by gene targeting experiments. In its present form, the manuscript links these proteins to B cell activation but does not convincingly back up the implied functional relevance to antigen/BCR endocytosis and/or trafficking leading to antigen presentation via MHC II.
• It should be explained why the proteomic experiments were conducted using anti-IgM antibodies as opposed to the more physiological stimulation via HEL antigen, used for the microscopy studies.
• Even though it is the central approach, the number of figures derived from the APEX2 proteomic experiments is quite high and should be condensed. For example, Figures 4 and 5 could be merged.
• Figure 1D/E and Figure S1C seem to be the same pictures.
• In contrast to Golga3, Vti1b is not mentioned in Figure 4 and the authors should explain why this particular protein was chosen for further investigation among all others (as opposed to proteins enriched upon anti-IgM treatment).
• In Figures 6 and S4, the most apparent changes in Golga3 staining appear to be the increased (cytoplasmic and peripheral) vesicle size and intensity. For the analysis and quantitation of peripheral Golga3 staining, a tubulin-based masking algorithm was used to segment the image. This raises three concerns: 1) The tubulin staining that was used for masking appears to be rather blurry and the expected microtubule network is barely visible. 2) More information is needed on how the masking algorithm treated Golga3 vesicles touching the mask border. Based on the images in S4, there seems to be substantial overlap between (visibly peripheral) Golga3 vesicles and tubulin, so this will likely have an impact on quantification results. 3) Authors should comment on the overall increase in Golga3 upon activation.

Minor Comments

• While the APEX2 construct is globally targeted into the lipid raft environment, the study uses this approach to investigate proteins that are in the proximity of the IgM-BCR. The authors mention in the discussion that there have been "challenges" to target the BCR directly. It may be beneficial to briefly discuss those problems the authors have been facing with.
• Figure 5B: It will be informative to show the BCR-induced (fold change) enrichment of Golga3 and Vti1b (and Kif20) in relation to IgM /kappa LC and the "classical" BCR signaling-related players.
• Figure 6AB: Please clearly indicate that unmasked images are displayed, but masked images were quantified for Golga3 staining.
• Figure 6CD: Since the quantification protocol of vesicle positioning involves nuclear staining, please depict respective DAPI stainings.
• Figure S1D: It should be indicated that AF633-streptavidin was used for the flow cytometry experiment in Figure S1D (x axis).

Significance

Overall, the presented study offers an interesting approach and provides a novel, unbiased view on BCR-mediated lipid raft dynamics. The method is appealing in its technicality and its presentation, and hence, might attract the attention of a larger community working on plasma membrane localization of signaling platforms. It proposes two candidate signaling proteins and verifies their BCR-dependent colocalization with lipid rafts and antigen. While Golga3 and Vti1b are novel and interesting target proteins in the context of BCR activation, a functional assessment of these proteins is not presented. Certainly, the article would greatly benefit from a follow-up investigation on the functional/physiological relevance of the proposed players. As it stands, the manuscript largely remains on the level of exploration.

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Referee #1

Evidence, reproducibility and clarity

This is an interesting study identifying membrane RAFT associated proteins in a mouse B cell line, before and after BCR stimulation, using a proximity biotinylation method. This method relies on the expression of an biotinylating enzyme APEX2 with a RAFT targeting domain that is activated by H2O2 addition. The system is well controlled by comparing transfected to non-transfected cells and by titrating H2O2 etc. The expected anti-IgM induced recruitment of the BCR to the RAFT domain is well documented in this system. The authors identify by proteome analysis over 1600 proteins in proximity to the membrane-targeted APEX2, most of which are constitutively labelled, i.e. do not change upon BCR stimulation. Only a minority of proteins (less than 100) changes dynamically between resting and stimulated state. Some results are surprising, as the authors discuss, as the known players of the BCR signalling pathway hardly change in their Raft association. Interesting is also the exclusion of signalling proteins such as Btk, BLNK and Ig-alpha/Ig-beta from BCR clusters upon activation. The strength of the system is that the APEX2 system causes a biotinylation with 1 min, which is an advantage to other systems and that the authors analyse 3 time points after BCR stimulation. The data are thoroughly analysed and discussed. The following points should be addressed: 1. Why did the authors not use the HEL antigen to stimulate their cells, as the A20 line expresses a Ag-specific BCR? Would this not be more physiological than Fab2-anti IgM? 2. Many proteins of pathways like RNA transport, Spliceosome, mRNA surveillance, mismatch repair etc. are identified. Although the authors try to explain some of these data, they should also consider unspecific labelling or unspecific enrichment of these proteins which have nothing to do with raft association. This should be more openly discussed. 3. The authors follow up two proteins that dynamically change during activation, Golga3 and Vti1b, and demonstrate their membrane association upon activation. This is of course relevant. What is missing, is some genetic studies. CRISPR-mediated KO is not difficult to do in cell lines. Have the authors produced such mutants for these two genes and analysed possible phenotypes in BCR signalling or other aspects? This would certainly strengthen the study.

Significance

This is a unique approach to globally identify proteins associated with the BCR in Rafts upon BCR stimulation. Comparable studies with other methods have been published before for B cell lines. Gupta et al. used quantitative proteomics of isolated RAFT-associated proteins before and after BCR stimulation. They also found that the association of most proteins to RAFTs was not changed after BCR stimulation. Saeki et al. used a proteomic approach in another B cell line to identify RAFT associated proteins, but without comparing stimulated to unstimulated cells. The approach used here has the advantage of not selecting only membrane bound proteins, but equally identifiying cytosolic proteins in vicinity to the Raft as well. Furthermore, dynamic changes are better analysed than in the other two studies. Therefore, the findings are relevant and a good advance in the field.

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Reply to the reviewers

Thank you for conducting the peer-review of our manuscript. We really appreciate the constructive criticism of the reviewers, and we are happy to note the positive appreciation of our core findings regarding the role of the decapping machinery during apical hook and lateral root formation and the identification of ASL9 as a target of the decapping machinery. However, both reviewers note we over-interpretate about the function of ASL9 in cytokinin and auxin responses which is not always supported by our data. Based on their feedback, we have toned down our claims and performed additional experiments and analyses and addressed all the comments raised by both reviewers. We hope this substantially revised and improved version of our manuscript will be better accepted.

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

In this manuscript, the authors describe the role of the mRNA decay machinery in apical hook formation during germination in darkness in A.thaliana. As reported, this machinery is predominantly described in literature in stress response processes, whereas little is known about its involvement during developmental processes. In detail, the authors demonstrated, via RNA immunoprecipitation (RIP) and genetic experiments, the direct regulation of the LATERAL ORGAN BOUNDARIES DOMAIN 3 (LBD3)/ASYMMETRIC LEAVES 2-19 LIKE 9 (ASL9) mRNA stability by the mRNA decapping machinery subunits DCPs. According to the manuscript, ASL9 controls apical hooking, LR development and primary root growth is regulating cytokinin signalling and hence its regulation helps to maintain a correct balance of auxin/cytokinin. Indeed, they showed an impair apical hooking and LR defects both in mRNA decapping mutants, where they observed more capped ASL9 compared to WT, and in ASL9 over-expressor lines. Moreover, they reported a largely restoration of over-expressor lines phenotype in the arr10-5arr12-1 double mutants. This work present simple but interesting data that corroborate the authors hypothesis.

Our response: We thank the reviewer for acknowledging the significance of our findings although we wonder what it´s meant by “simple data”. Through a combination of (complicated) genetics, phenotyping, cell imaging and molecular biology, we have provided mechanistic evidence on the function of the decapping machinery during 2 different post embryonic developmental events. Please see our detailed answers to the reviewer’s comments in the following.

Nonetheless, I have both major comments and minor comments to improve the manuscript: MAJOR COMMENTS: 1. I am a bit concerned by the fact that cytokinin, auxin, LBD3, ARR12 and ARR10 have been largely involved in vasculature development and that the obtained results might be due to their role in vasculature development more than in LBD3 mRNA decapping process. Authors should provide evidence that their results are independent from vasculature defects present in those backgrounds or in case discuss this possibility.

__Our response: __We are a bit puzzled on how vasculature development could explain the apical hook phenotype observed in the decapping mutant. Data like the rapid assembly of P-bodies upon IAA (Fig. 3C) treatments and the overall decreased DR5 signal in dcp mutants (Fig.S5&6) are all consistent with a process precluding vasculature formation. However, we still discuss the possibility that the developmental defects observed in mRNA decapping mutants and ASL9 overexpressor might be related to the vasculature development in these plants (Line 239-244).

The interaction between the described players and auxin is not clear. From the reported experiments it is difficult to understand what authors wants to report as in S4 and S5 are reported experiments not fully described in the text (authors report about introgression of DR5::GFP in dcp1 and 2 mutants, but SD4 reports ACC treatments of DR5::GFP,dcp2 mutants and SD5 of 7 dpg root meristems of this strain ). Please describe and discuss better the experiment. Also, to this reviewer it is difficult to understand whether the absence of auxin activity in the dcp2 mutants hypocotyl is merely an effect of the lack of the hook formation in this background or a cause. Please clarify this point including new experiments (axr1 or axr3 mutants might help in understand this point).

__Our response: __We follow the reviewer’s suggestions and trust we now describe and discuss Fig S5&6 (old Fig S4&S5) clear in Line 188-193. As axr1 has been published with apical hook and lateral root defect (old Line 42, new Line 39&169), we did not repeat it in new experiments but emphasize it in Line 169.

Authors conclude that mRNA decapping is also involved in root growth. However, they do not report direct evidences regarding root growth but mostly regarding the mere root lenght at a precise developmental stage. Please eliminate this point or provide new experiments (e.g., root length and root meristem activity over time)

__Our response: __We follow the reviewer’s suggestions and eliminate the data regarding to primary root growth (Fig. 3-6 &S2)

Regarding root growth defects, these might be due to defect in the vasculature development, please analyse this point or report new experiments (e.g., vasculature analysis of dcp1,2 mutants or tissue specific expression of DCP2).

__Our response: __We largely agree with the reviewer, all the decapping components DCP1, DCP2, DCP5 and PAT1 exhibit high expression in xylem cells and low expression in procambium cells (Brady et al., 2007) indicating functions of decapping components in vasculature development. However, we did not include this knowledge in our manuscript since we decided to eliminate the primary root growth data (Fig.3-6&S2).

For consistency the last paragraph of result section: "ASL9 directly contributes to apical hooking, LR formation and primary root growth" should be part of the result section entitled "Accumulation of ASL9 suppresses LR formation and primary root growth". Authors should move this result in the paragraph before "Interference of a cytokinin pathway and/or exogenous auxin restores developmental defects of ASL9 over-expressor and mRNA decay deficient mutants".

__Our response: __We agree thus we reorganize the result sections and move "ASL9 directly contributes to apical hooking and LR formation" before "Interference of a cytokinin pathway and/or exogenous auxin restores developmental defects of ASL9 over-expressor and mRNA decay deficient mutants" (Line 152).

I suggest being consistent in the description of the statistical analysis. In particular: - I suggest reporting the meaning of ANOVA letters and the P-value in each figure as sometimes these information are missing, especially in Fig.2.

__Our response: __We used ANOVA letters when comparing among genotypes and treatments, for example Fig 2A; and we used stars when comparing to controls, for example old Fig 2F. For consistency, we use letters for all the statistical analysis now and we report the meaning of the letters clearly in the figure legends (Fig. 1-6, S1-5&7). However, we think that putting the P-values in each figure would not be reader-friendly, and thus we have not done this.

• in Fig.S3 please report the statistical significance on bars and the statistical analysis performed.

__Our response: __We thank the reviewer for pointing it out, we report the statistical analysis now in new Fig. S2 (old Fig. S3).

MINOR COMMENTS: L31- please replace "normal" with "proper"

__Our response: __We thank the reviewer for the suggestion, now we replace "normal" with "proper"(Line 30)

L42-please report the acronym of axr1

__Our response: __The acronym of axr1 is correctly reported (Line 40).

L57, L59-please include the entire name of DCP2 and XRN

__Our response: __The entire name of DCP2 and XRN are correctly included (Line 55 &57).

-Please report how many plants were analysed in legend or in methods section

__Our response: __The numbers of plants in analysis are now reported in figure legends (Fig. 1-6, S1,2&7).

-Please report how many transgenic independent lines were obtained in methods section

__Our response: __The numbers of transgenic independent lines are now reported in methods (Line 292)

• Please, try to change the colours of the graph in Fig.S2A-B, as it quite difficult to distinguish light grey shades.

__Our response: __We thank the reviewer’s suggestions, the colours of new Fig.S3&4 (old Fig.S2) are changed.

• In Fig. 5A and S5A scale bars are missing.

__Our response: __We thank the reviewer for pointing this out, scale bars are correctly added in new Fig 4 &S6 (old Fig 5 &S5).

Reviewer #1 (Significance (Required)): The manuscript is interesting and analyse important and overlooked aspects of the role of mRNA decapping in development. Nonetheless experiments reported are not particularly innovative and not always sound. Also authors analysis are a bit superficial probably because they decide to utilize too many systems in their research (root development, hook development and lateral root development).

Our response: We thank the reviewer again for acknowledging the significance of our findings and hope we satisfied the reviewer with our answers above. However, we would like to ask what is the purpose of writing “experiments are not particularly innovative”? We admit we used established and robust experiments which we found sufficient to answer the overlooked aspects of the role of mRNA decpping in apical hook and lateral root development as also noted by the reviewer, but maybe we simply don't understand the comment.

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

Major Comments 1. My main concern is about the authors' conclusions on the role of mRNA decay and ASL9/LBD3 in the control over cytokinin and auxin responses. I don't think that based on the data presented the authors may do the conclusions stated on lines 184-185, see also the points below.

__Our response: __We agree thus we tone down our conclusion in our new manuscript (Line 197-199), see answers below for detail.

The conclusion about the role of ASL9 and its direct involvement in the apical hook formation and lateral root development/main root growth is a bit exaggerated, based on rather tiny effects mediated by the introduction of asl9-1 into the dcp5-1. Rather, the data suggest that misregulation of other transcripts in the mRNA decay-deficient lines might be responsible for the observed defects. That is also apparent from slightly different phenotypes seen in dcp5-1/pat triple compared to oxASL9 (Fig. 3A). The strong dependency of oxASL9 phenotype on the presence of functional ARR10 and ARR12 implies cytokinin signaling-dependent mechanism of ASL9/LBD3 action (see also point 3 below). Considering the aforementioned phenotype differences between the dcp5-1/pat triple and oxASL9, it would be interesting to see the possible dependence of the mRNA decay-deficient line phenotypes on the cytokinin signaling, too.

__Our response: __We note restoration of dcp5-1 developmental defects in asl9 backgrounds is partial, indicating other ASLs or non-ASLs also contributing to apical hook and lateral root development (old Line 224-225, new Line 229-230 &234-235). We also note that partial suppression is a common phenomenon when studying discrete developmental traits. Two such examples could include the knockout of TPXL5 which partially suppressed the increase of LR density in the hy5 mutant and the introduction of a point mutation in SnRK2.6 in the gsnor1-3/ost1-3 double-mutant partially suppressed the effect of gsnor1-3 on ABA-induced stomatal closure (Qian et al., 2022 The Plant Cell doi.org/10.1093/plcell/koac358; Wang et al., 2015 PNAS 112, 613). In addition to such discrete developmental traits, more dramatic phenotypes like autoimmunity may also only be partially suppressed (Zhang et al., 2012 CH&M 11, 253). However, we agree that it’s interesting to check the dependence of cytokinin signaling of the developmental defects in mRNA decay-deficient mutants. Unfortunately, we were only able to cross arr10 arr12 into dcp5-1. This line showed similar partial restoration of dcp5-1 developmental defects as seen for dcp5-1asl9-1. Overall, these data indicates that contribution of mRNA decapping targeting ASL9 transcripts during apical hook and LR formation depends on ARR10 and ARR12 (Fig. 4&6, Line 180-186).

Also the hypothesis on the upregulation of cytokinin signaling in the mRNA decay mutants and Col-0/oxASL9 is very indirect and should be tested using e.g. TCSn:GFP. The type A ARRs (RRAs) are not only the negative regulators of cytokinin signaling, but also the cytokinin primary response genes. Thus, the downregulation of RRAs could mean the downregulation of the cytokinin signaling pathway in the mRNA decay mutants and/or Col-0/oxASL9. The latter seems to be the case as shown recently (Ye et al., 2021).

__Our response: __We thank the reviewer for suggesting a different annotation of our result regarding to type-A ARRs. Ye et al reported accumulation of ASL9/LBD3 induced downregulation of cytokinin pathway based on weaker ARR5 and TCSn-GFP signal(Ye et al., 2021). However, the fact that knocking out cytokinin signaling activator genes ARR10 and ARR12 largely restored developmental defects in ASL9 over-expressors lead to the hypothesis of upregulated cytokinin signaling in ASL9 over-expressors (Fig 5). Therefore, we substitute “upregulation” with “misregulation” for cytokinin signaling to compromise in our new manuscript (Line 174).

The hypothesis on the causal link between the observed auxin-related defects and upregulated cytokinin signaling (Discussion, lines 214-216) is more than speculation. This could be tested by introducing arr10 arr12 into the dcp2-1/DR5-GFP and/or dcp5-1/DR5-GFP.

__Our response: __We thank the reviewer for the suggestions, due to time and funds management, we decided to check auxin related gene expression in dcp5-1arr10-5arr12-1 mutants instead of making transgenic plants in triple mutant. The repressed expression of SAUR23 and TAR2 in dcp5-1 is partially restored (Fig. S4), indicating possible repression of auxin signaling caused by upregulated cytokinin signaling. However, for consistency in cytokinin signaling description, we tone down the hypothesis on the link between auxin-related defects and cytokinin signaling (Line 218-220).

Compared to the text/quantification of the effect of asl9-1 mutant on the hook formation (Fig. S1D), I see exaggerated hook formation both in the presence and absence of ACC in asl9-1, at least on the figures shown in Fig. S1C. Are the shown seedlings not representative?

__Our response: __We thank the reviewer for pointing our mistakes out, the shown seedlings are representative but mislabeled and the mistakes are corrected now in our new manuscript (Fig. S1C).

Minor Comments 1. Syntax problem in the sentence on lines 45-46 (?).

__Our response: __We thank the reviewer for pointing it out, syntax problem of this sentence is solved now in new manuscript (Line 41-44).

The sentence on lines 48-49 should be rephrased. It implies the cytokinins regulate the amount of RRBs, which is not correct (cytokinins control phosphorylation of RRBs, not their abundance, RRAs are not TFs).

__Our response: __We now rephrase the sentence in a correct way (Line 46)

In the FL for Fig. 2F there is mentioned that MYC-YFP was used as a control compared to the main text mentioning YFP-WAVE (?).

__Our response: __We thank the reviewer for pointing this out, the YFP-WAVE line we used is MYC-YFP transgenic plants, we now include this information in our manuscript (Line 136) and for consistency we changed MYC-YFP to YFP-WAVE in Fig. 2F.

Naito et al. (2007) suggest ASL9 as a target of cytokinin signaling, but I don't think they imply the involvement of ASL9 in the cytokinin signaling as mentioned e.g. on line 166 (?)

__Our response: __We largely agree with the reviewer thus we also cite Ye’s paper here in our new manuscript (Line 165)

References Ye L, Wang X, Lyu M, Siligato R, Eswaran G, Vainio L, Blomster T, Zhang J, Mahonen AP. 2021. Cytokinins initiate secondary growth in the Arabidopsis root through a set of LBD genes. Curr Biol 31(15): 3365-3373 e3367.

Reviewer #2 (Significance (Required)):

The authors provide interesting data suggesting possible role of mRNA decay machinery in the hook and lateral root formation and main root growth via decapping-mediated control over ASL9/LBD3 transcript abundance. Based on the observed interaction of the observed phenotypes with hormonal regulations, the authors' conclude mechanistic link between the mRNA decay/ASL9 and cytokinin and auxin responses.

Our response: We thank the reviewer for acknowledging the significance of our findings.

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Referee #2

Evidence, reproducibility and clarity

Major Comments

1. My main concern is about the authors' conclusions on the role of mRNA decay and ASL9/LBD3 in the control over cytokinin and auxin responses. I don't think that based on the data presented the authors may do the conclusions stated on lines 184-185, see also the points below.
2. The conclusion about the role of ASL9 and its direct involvement in the apical hook formation and lateral root development/main root growth is a bit exaggerated, based on rather tiny effects mediated by the introduction of asl9-1 into the dcp5-1. Rather, the data suggest that misregulation of other transcripts in the mRNA decay-deficient lines might be responsible for the observed defects. That is also apparent from slightly different phenotypes seen in dcp5-1/pat triple compared to oxASL9 (Fig. 3A). The strong dependency of oxASL9 phenotype on the presence of functional ARR10 and ARR12 implies cytokinin signaling-dependent mechanism of ASL9/LBD3 action (see also point 3 below). Considering the aforementioned phenotype differences between the dcp5-1/pat triple and oxASL9, it would be interesting to see the possible dependence of the mRNA decay-deficient line phenotypes on the cytokinin signaling, too.
3. Also the hypothesis on the upregulation of cytokinin signaling in the mRNA decay mutants and Col-0/oxASL9 is very indirect and should be tested using e.g. TCSn:GFP. The type A ARRs (RRAs) are not only the negative regulators of cytokinin signaling, but also the cytokinin primary response genes. Thus, the downregulation of RRAs could mean the downregulation of the cytokinin signaling pathway in the mRNA decay mutants and/or Col-0/oxASL9. The latter seems to be the case as shown recently (Ye et al., 2021).
4. The hypothesis on the causal link between the observed auxin-related defects and upregulated cytokinin signaling (Discussion, lines 214-216) is more than speculation. This could be tested by introducing arr10 arr12 into the dcp2-1/DR5-GFP and/or dcp5-1/DR5-GFP.
5. Compared to the text/quantification of the effect of asl9-1 mutant on the hook formation (Fig. S1D), I see exaggerated hook formation both in the presence and absence of ACC in asl9-1, at least on the figures shown in Fig. S1C. Are the shown seedlings not representative?

Minor Comments

1. Syntax problem in the sentence on lines 45-46 (?).
2. The sentence on lines 48-49 should be rephrased. It implies the cytokinins regulate the amount of RRBs, which is not correct (cytokinins control phosphorylation of RRBs, not their abundance, RRAs are not TFs).
3. In the FL for Fig. 2F there is mentioned that MYC-YFP was used as a control compared to the main text mentioning YFP-WAVE (?).
4. Naito et al. (2007) suggest ASL9 as a target of cytokinin signaling, but I don't think they imply the involvement of ASL9 in the cytokinin signaling as mentioned e.g. on line 166 (?)

References

Ye L, Wang X, Lyu M, Siligato R, Eswaran G, Vainio L, Blomster T, Zhang J, Mahonen AP. 2021. Cytokinins initiate secondary growth in the Arabidopsis root through a set of LBD genes. Curr Biol 31(15): 3365-3373 e3367.

Significance

The authors provide interesting data suggesting possible role of mRNA decay machinery in the hook and lateral root formation and main root growth via decapping-mediated control over ASL9/LBD3 transcript abundance. Based on the observed interaction of the observed phenotypes with hormonal regulations, the authors' conclude mechanistic link between the mRNA decay/ASL9 and cytokinin and auxin responses.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, the authors describe the role of the mRNA decay machinery in apical hook formation during germination in darkness in A.thaliana. As reported, this machinery is predominantly described in literature in stress response processes, whereas little is known about its involvement during developmental processes. In detail, the authors demonstrated, via RNA immunoprecipitation (RIP) and genetic experiments, the direct regulation of the LATERAL ORGAN BOUNDARIES DOMAIN 3 (LBD3)/ASYMMETRIC LEAVES 2-19 LIKE 9 (ASL9) mRNA stability by the mRNA decapping machinery subunits DCPs. According to the manuscript, ASL9 controls apical hooking, LR development and primary root growthis regulating cytokinin signalling and hence its regulation helps to maintain a correct balance of auxin/cytokinin. Indeed, they showed an impair apical hooking and LR defects both in mRNA decapping mutants, where they observed more capped ASL9 compared to WT, and in ASL9 over-expressor lines. Moreover, they reported a largely restoration of over-expressor lines phenotype in the arr10-5arr12-1 double mutants.

This work present simple but interesting data that corroborate the authors hypothesis. Nonetheless, I have both major comments and minor comments to improve the manuscript:

Major comments

1. I am a bit concerned by the fact that cytokinin, auxin, LBD3,ARR12 and ARR10 have been largely involved in vasculature development and that the obtained results might be due to their role in vasculature development more than in LBD3 mRNA decapping process. Authors should provide evidence that their results are independent from vasculature defects present in those backgrounds or in case discuss this possibility.
2. The interaction between the described players and auxin is not clear. From the reported experiments it is difficult to understand what authors wants to report as in S4 and S5 are reported experiments not fully described in the text (authors report about introgression of DR5::GFP in dcp1 and 2 mutants, but SD4 reports ACC treatments of DR5::GFP,dcp2 mutants and SD5 of 7 dpg root meristems of this strain ). Please describe and discuss better the experiment. Also, to this reviewer it is difficult to understand whether the absence of auxin activity in the dcp2 mutants hypocotyl is merely an effect of the lack of the hook formation in this background or a cause. Please clarify this point including new experiments (axr1 or axr3 mutants might help in understand this point).
3. Authors conclude that mRNA decapping is also involved in root growth. However, they do not report direct evidences regarding root growth but mostly regarding the mere root lenght at a precise developmental stage. Please eliminate this point or provide new experiments (e.g., root length and root meristem activity over time)
4. Regarding root growth defects, these might be due to defect in the vasculature development, please analyse this point or report new experiments (e.g., vasculature analysis of dcp1,2 mutants or tissue specific expression of DCP2).
5. For consistency the last paragraph of result section: "ASL9 directly contributes to apical hooking, LR formation and primary root growth" should be part of the result section entitled "Accumulation of ASL9 suppresses LR formation and primary root growth". Authors should move this result in the paragraph before "Interference of a cytokinin pathway and/or exogenous auxin restores developmental defects of ASL9 over-expressor and mRNA decay deficient mutants".
6. I suggest being consistent in the description of the statistical analysis. In particular:
   • I suggest reporting the meaning of ANOVA letters and the P-value in each figure as sometimes these information are missing, especially in Fig.2.
   • in Fig.S3 please report the statistical significance on bars and the statistical analysis performed.

Minor comments

L31- please replace "normal" with "proper"

L42-please report the acronym of axr1

L57, L59-please include the entire name of DCP2 and XRN

• Please report how many plants were analysed in legend or in methods section
• Please report how many transgenic independent lines were obtained in methods section
• Please, try to change the colours of the graph in Fig.S2A-B, as it quite difficult to distinguish light grey shades.
• In Fig. 5A and S5A scale bars are missing.

Significance

The manuscript is interesting and analyse important and overlooked aspects of the role of mRNA decapping in development. Nonetheless experiments reported are not particularly innovative and not always sound. Also authors analysis are a bit superficial probably because they decide to utilize too many systems in their research (root development, hook development and lateral root development).

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Reply to the reviewers

Revision Plan

Manuscript number: RC-2022-01765

Corresponding author(s): Dr. Huiqing Zhou (Radboud University)

1. General Statements [optional]

We like to thank the editor and reviewers for their constructive comments and suggestions for improving the manuscript. We here address the comments point-by-point using the template of the revision plan.

2. Description of the planned revisions

Reviewer #1:

• While the study is complete and describes well, a strong conclusion, including validation of the role of some TFs such as FOSL2 through knock out experiments in model organisms or cell culture will elevate the paper more (optional). *

To address this point, we will perform siRNA knockdown experiments of TFs identified in our study, including FOSL2, in primary LSCs, and examine the transcriptional consequences of knocking down these TFs by RNA-seq or RT-qPCR analyses.

Reviewer #2:

1. • The findings provide an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. Although the presented predictions are interesting, what is missing is an examination of the functional significance of the findings. * Indeed, we fully agree with the reviewer that additional functional examinations are important and relevant and would strengthen the manuscript. We propose to do the following functional analyses to further demonstrate the importance of the key TFs.

2. Immunostaining of the key TFs in the human cornea and in LSCs and KCs.

3. As described above, we will perform siRNA experiments for key TFs identified in our study, followed by RNA-seq or RT-qPCR analysis, to assess the transcriptional program controlled by these key TFs.

4. The gene regulatory network controlled by these tested TFs will be analysed, to examine the interplay of these TFs in transcriptional regulation and in cell fate determination. Reviewer #2:

5. Also, the findings indicate an interaction between FOXL2 and other TFS is important for maintaining the corneal epithelium. These interesting predictions indicate an important role for FoxL2 in corneal function. It would be important to verify these predictions by experimental studies, for example, by presenting the association of FOXL2 with the predicted co-factors and presenting data on the effect of the identified mutation on FOXL2 transcriptional activity.

*

We assume that Reviewer #2 refers to FOSL2 instead of FOXL2. We agree with this reviewer’s suggestion to functionally address the importance of FOSL2 in the cornea. In order to answer this, we plan to perform FOSL2 staining and FOSL2 siRNA knockdown in LSCs, followed by RNA-seq, as described above. This will show the FOSL2 importance in LSCs and in cornea, and will identify the affected downstream gene networks.

Regarding the clinical effect of the specific FOSL2 variant reported in our study, we agree that functional validation would strengthen our work even more. We believe that the main message of the study is the use of integrative omics analyses to uncover new transcription factors involved in corneal and limbal fates, and to highlight new candidate genes in corneal disease. Therefore we feel that the disease mechanism behind the specific FOSL2 variant, albeit interesting, is beyond the scope of this study. Nonetheless, we reinforced the pathogenicity of the variant with various in silico prediction platforms (supplementary table 9). Interestingly, a recent study reported that FOSL2 truncating mutations are involved in a new syndrome with ectodermal defects and cataract. This is in line with our findings that FOSL2 is an important shared TF in both LSCs and KCs, and strengthens the predicted role of FOSL2 in the epithelium of the eye and associated diseases. We have included additional discussion on this study in the Discussion line 662-668.

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

Reviewer #2:

In Figure 1, the authors compare the transcriptome and epigenome (ATAC-seq and histone modifications) of basal KCs from skin donors and cultured LSCs established from limbal biopsies. The authors should clarify the source of the cells in the published studies - specifically, why more data were needed and if these were comparable to their datasets.

We have included the cell sources and cultured conditions from the published studies and added additional columns in the supplementary tables 1, 2 and 3. Briefly, LSC publicly available samples were extracted from post-mortem cornea and cultured in DMEM/F12, or KSFM.

Regarding the questions on the necessity of incorporating more data, our reasoning was two-fold. First of all, we have taken an integrated approach to perform our analysis, using both our own and publicly available datasets. We see this as a strength, as the most important differences between cell types that determine cell fates should be consistent with cells generated from different donors and labs. Second, we choose to generate more data in our own lab in order to make sure to have comparisons without the influence of technical differences between publicly available datasets. We include text about this approach in the Discussion (lines) 578-580. Furthermore, to show that the datasets we used are consistent and can be integrated, we have performed a PCA correlation analysis for the RNA-seq analysis (supplementary figures 1A&1B lines 834-837), and added a spearman correlation analysis for the ATAC-seq datasets (supplementary figure 5F & lines 818-820). Both indicated clear biological signal similarities between cell types across different labs and techniques.

Reviewer #2:

3.Next, they compared the transcriptomes of LSCs and KCs to the transcription profile of LSCs from two aniridia patients and control. They need to specify the stage of the donors' disease and provide details on the control samples.

Both aniridia samples were from patients of stage 4 on the Lagali Stages (Lagali, N. et al. (2020) ‘Early phenotypic features of aniridia-associated keratopathy and association with PAX6 coding mutations’, The Ocular Surface, 18(1), pp. 130–140. We have included this information in Material and Methods (lines 738-739). For healthy control cells, no information regarding the stage and gender is available, as they are from anonymous individuals. We added more information on the aniridia and control samples regarding the culture conditions and passage numbers (lines 747:750).

Reviewer #2:

• In addition, and as indicated above, when combining published datasets, one should clarify whether the methods of collecting/growing the cells and the disease stage are comparable. This is important with samples from aniridia as it is unclear if the patient LSCs survive the isolation or if other cells take over.*

Healthy LSC cells used in the direct comparison with aniridia LSC cells were grown using the same expansion and culture conditions. Furthermore, the method of culture, extraction and expansion between the earlier published aniridia cell data and our data are exactly the same (lines 735:750). As described above, we have included the cell sources from the aniridia samples, and added additional columns in the supplementary table 1.

Reviewer #2:

• It would be valuable to the community if the presented data were also provided online in a web tool so that CRE activity or gene expression could be easily examined.*

We have expanded the UCSC track hub to highlight the identified variable CRE elements. This will enable a searchable tool for differential CREs close to genes of interest between KCs and LSCs. We have furthermore added a sentence to explicitly mention the presence of this track hub in the result section (lines 248-249).

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

Reviewer #1:

1. By identifying differential cis regulatory elements in two cells, they identify TFs that are associated with overexpression or repression of genes of interest. However, this approach of relying solely upon nearest genes of CREs is very cursory and the authors could have used methods such as Activity-by-Contact to establish CREs and their target genes and then assessed their correlation with expression (optional). Activity-by-Contact incorporation would be an exciting inclusion in the data analysis, and for the next step in GRN modelling. However, this is out of the scope of this manuscript. In addition, we would like to point out that we did not solely rely on the method of mapping CREs to the nearest genes. Instead, for H3K27ac and ATAC-seq signals, our analysis uses a weighted TSS distance method, within windows of up to 100kb, similar to the method ANANSE and other published gene regulatory network tools. For H3K4me3 and H3K27me3 marks which correlate far better with an expression of the closest genes, we use a window of 2kb at the closest gene.

Reviewer #2:

When ATAC-seq was combined with histone modification analyses, about a third of these regions showed different characteristics, inferring tissue-specific activities. These data may be valuable for identifying tissue-specific cis-regulatory elements (CREs) for the key TFs. This, however, remains to be examined experimentally.

It is not fully clear to us what ‘experimentally examination’ was referred to by this reviewer, whether to test these tissue-specific CREs individually or globally. We agree that it is important to test tissue-specific CREs experimentally to examine their function, e.g., which genes they are regulating, and which role they play in tissue-specificity. However, this is out of the scope of this manuscript.

---

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

Multi-omics analyses identify transcription factor interplay in corneal epithelial fate determination and disease The authors of this manuscript describe their work on identifying transcriptional regulators and their interplay in cornea using limbal stem cells and epidermic using keratinocytes. This is a very well written and well described comprehensive manuscript. The authors performed various analyses which were in line with logical workflow of the research question. The authors begin by first identifying differential gene expression signals for the two tissues along with enriched biological processes using GSEA and PROGENy. The strength of this manuscript also includes usage of epigenetic data to determine the cell fate and its drivers. The authors study various epigenetic assays and correlate them expression levels of TFs and genes to identify regulatory patterns that mark differences between LSCs and KCs. By identifying differential cis regulatory elements in two cells, they identify TFs that are associated with overexpression or repression of genes of interest. However, this approach of relying solely upon nearest genes of CREs is very cursory and the authors could have used methods such as Activity-by-Contact to establish CREs and their target genes and then assessed their correlation with expression (optional). In logical progression, the authors use gene regulatory networks using to compare LSC and KC with Embryonic Stem Cells (ESC) to identify most influential TFs to differentiate them. Along with identifying key TFs, they also identify TF regulatory hierarchy to find TFs that regulate other TFs in context-specific manner. They identify "p63, FOSL2, EHF, TFAP2A, KLF5, RUNX1, CEBPD, and FOXC1 are among the shared epithelial TFs for both LSCs and KCs. PAX6, SMAD3, OTX1, ELF3, and PPARD are LSC specific TFs for the LSC fate, and HOXA9, IRX4, CEBPA, and GATA3 were identified as KC specific TFs." And "p63, KLF4 and TFAP2A can potentially co-regulate PAX6 in LSCs." To compare in vitro findings with in vivo results, they also generate single cell data and identify specific TFs that may play pathobiological role in disease development and progression. While the study is complete and describes well, a strong conclusion, including validation of role of some TFs such as FOSL2 through knock out experiments in model organisms or cell culture will elevate the paper more (optional). This study merits publication in high quality journal (IF:10-15)

Reviewer #1 (Significance (Required)):

The study is very significant not only in the context of corneal disease biology. The imbalance in interplay of TFs is often envisaged behind disease development but very few efforts of detailed analysis are undertaken. This study is performed very well and the methods are described in clear manner. Appropriate statistical methods are used where required.

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

The study by Smits et al. presents detailed multi-omics (transcripts, ATAC-seq, histone marks) analyses comparing human limbal stem cells (LSCs) to skin keratinocytes (KCs). The authors compared these two cell types because they have a shared origin in the epidermal progenitors and because LSC diseases occasionally accompany a transition to KC-like phenotypes. The authors analyzed the "omics" data using several bioinformatic analysis tools. Their analyses resulted in a detailed list of the critical transcription factors (TFs) and their gene regulatory networks shared between the two lineages and those unique to either LSCs or KCs.

The findings provide an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. Although the presented predictions are interesting, what is missing is an examination of the functional significance of the findings. Also, as detailed below, there is a need to clarify the source of the cells used for the different analyses.

Comments and suggestions: 1. In Figure 1, the authors compare the transcriptome and epigenome (ATAC-seq and histone modifications) of basal KCs from skin donors and cultured LSCs established from limbal biopsies. The authors should clarify the source of the cells in the published studies - specifically, why more data were needed and if these were comparable to their datasets. 2. Next, they compared the transcriptomes of LSCs and KCs to the transcription profile of LSCs from two aniridia patients and control. They need to specify the stage of the donors' disease and provide details on the control samples. In addition, and as indicated above, when combining published datasets, one should clarify whether the methods of collecting/growing the cells and the disease stage are comparable. This is important with samples from aniridia as it is unclear if the patient LSCs survive the isolation or if other cells take over. The finding that LSC genes are reduced in aniridic LSCs may suggest that the cells resemble KCs, although specific KC genes are not elevated. 3. Figure 2: The authors characterized the regulatory regions in the two cell types based on ATAC-seq and histone marks. Based on ATAC-seq, 80% of the open areas were shared between the two lineages. When ATAC-seq was combined with histone modification analyses, about a third of these regions showed different characteristics, inferring tissue-specific activities. These data may be valuable for identifying tissue-specific cis-regulatory elements (CREs) for the key TFs. This, however, remains to be examined experimentally. 4. It would be valuable to the community if the presented data were also provided online in a web tool so that CRE activity or gene expression could be easily examined. 5. Using motif predictions, the authors point to the TF families that likely control the differential CREs (Figure 3). Next, the authors constructed the gene regulatory network based on the (ANANSE) pipeline, which integrates CRE and TF motif predictions with the expression of TFs and their target genes. To gain further insight into the shared gene regulatory networks, they compared each to similar data from embryonic stem cells. Their analysis further suggests shared TFs regulating each other and some of the tissue-specific transcription factors. Differential gene expression of the TFs was partially validated by analyzing available single-cell data (Figure 4). 6. In the final section of the study, the authors aimed to identify TFs in LSCs that are relevant to corneal disease. They examined whether the LSC TFs are bound to genes associated with LSC deficiency and inherited corneal diseases. To accomplish this task, the authors incorporated single-cell data on corneal gene expression and available datasets on genetic analyses of families. Through this analysis, they identified a mutation in FOSL2 that may be causing corneal opacity in the carriers. Also, the findings indicate an interaction between FOXL2 and other TFS is important for maintaining the corneal epithelium. These interesting predictions indicate an important role for FoxL2 in corneal function. It would be important to verify these predictions by experimental studies, for example, by presenting the association of FOXL2 with the predicted co-factors and presenting data on the effect of the identified mutation on FOXL2 transcriptional activity.

Reviewer #2 (Significance (Required)):

The analysis provides an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. The results predict a role for FoxL2 in corneal function.

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

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The study by Smits et al. presents detailed multi-omics (transcripts, ATAC-seq, histone marks) analyses comparing human limbal stem cells (LSCs) to skin keratinocytes (KCs). The authors compared these two cell types because they have a shared origin in the epidermal progenitors and because LSC diseases occasionally accompany a transition to KC-like phenotypes. The authors analyzed the "omics" data using several bioinformatic analysis tools. Their analyses resulted in a detailed list of the critical transcription factors (TFs) and their gene regulatory networks shared between the two lineages and those unique to either LSCs or KCs.

The findings provide an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. Although the presented predictions are interesting, what is missing is an examination of the functional significance of the findings. Also, as detailed below, there is a need to clarify the source of the cells used for the different analyses.

Comments and suggestions:

1. In Figure 1, the authors compare the transcriptome and epigenome (ATAC-seq and histone modifications) of basal KCs from skin donors and cultured LSCs established from limbal biopsies. The authors should clarify the source of the cells in the published studies - specifically, why more data were needed and if these were comparable to their datasets.
2. Next, they compared the transcriptomes of LSCs and KCs to the transcription profile of LSCs from two aniridia patients and control. They need to specify the stage of the donors' disease and provide details on the control samples. In addition, and as indicated above, when combining published datasets, one should clarify whether the methods of collecting/growing the cells and the disease stage are comparable. This is important with samples from aniridia as it is unclear if the patient LSCs survive the isolation or if other cells take over. The finding that LSC genes are reduced in aniridic LSCs may suggest that the cells resemble KCs, although specific KC genes are not elevated.
3. Figure 2: The authors characterized the regulatory regions in the two cell types based on ATAC-seq and histone marks. Based on ATAC-seq, 80% of the open areas were shared between the two lineages. When ATAC-seq was combined with histone modification analyses, about a third of these regions showed different characteristics, inferring tissue-specific activities. These data may be valuable for identifying tissue-specific cis-regulatory elements (CREs) for the key TFs. This, however, remains to be examined experimentally.
4. It would be valuable to the community if the presented data were also provided online in a web tool so that CRE activity or gene expression could be easily examined.
5. Using motif predictions, the authors point to the TF families that likely control the differential CREs (Figure 3). Next, the authors constructed the gene regulatory network based on the (ANANSE) pipeline, which integrates CRE and TF motif predictions with the expression of TFs and their target genes. To gain further insight into the shared gene regulatory networks, they compared each to similar data from embryonic stem cells. Their analysis further suggests shared TFs regulating each other and some of the tissue-specific transcription factors. Differential gene expression of the TFs was partially validated by analyzing available single-cell data (Figure 4).
6. In the final section of the study, the authors aimed to identify TFs in LSCs that are relevant to corneal disease. They examined whether the LSC TFs are bound to genes associated with LSC deficiency and inherited corneal diseases. To accomplish this task, the authors incorporated single-cell data on corneal gene expression and available datasets on genetic analyses of families. Through this analysis, they identified a mutation in FOSL2 that may be causing corneal opacity in the carriers. Also, the findings indicate an interaction between FOXL2 and other TFS is important for maintaining the corneal epithelium. These interesting predictions indicate an important role for FoxL2 in corneal function. It would be important to verify these predictions by experimental studies, for example, by presenting the association of FOXL2 with the predicted co-factors and presenting data on the effect of the identified mutation on FOXL2 transcriptional activity.

Significance

The analysis provides an overview of transcriptional regulators and targets in two essential tissues. This is a valuable tool for future discoveries regarding the processes governing cell differentiation and those involved in the disease mechanism of the cornea. The results predict a role for FoxL2 in corneal function.

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

Multi-omics analyses identify transcription factor interplay in corneal epithelial fate determination and disease The authors of this manuscript describe their work on identifying transcriptional regulators and their interplay in cornea using limbal stem cells and epidermic using keratinocytes. This is a very well written and well described comprehensive manuscript. The authors performed various analyses which were in line with logical workflow of the research question. The authors begin by first identifying differential gene expression signals for the two tissues along with enriched biological processes using GSEA and PROGENy. The strength of this manuscript also includes usage of epigenetic data to determine the cell fate and its drivers. The authors study various epigenetic assays and correlate them expression levels of TFs and genes to identify regulatory patterns that mark differences between LSCs and KCs. By identifying differential cis regulatory elements in two cells, they identify TFs that are associated with overexpression or repression of genes of interest. However, this approach of relying solely upon nearest genes of CREs is very cursory and the authors could have used methods such as Activity-by-Contact to establish CREs and their target genes and then assessed their correlation with expression (optional). In logical progression, the authors use gene regulatory networks using to compare LSC and KC with Embryonic Stem Cells (ESC) to identify most influential TFs to differentiate them. Along with identifying key TFs, they also identify TF regulatory hierarchy to find TFs that regulate other TFs in context-specific manner. They identify "p63, FOSL2, EHF, TFAP2A, KLF5, RUNX1, CEBPD, and FOXC1 are among the shared epithelial TFs for both LSCs and KCs. PAX6, SMAD3, OTX1, ELF3, and PPARD are LSC specific TFs for the LSC fate, and HOXA9, IRX4, CEBPA, and GATA3 were identified as KC specific TFs." And "p63, KLF4 and TFAP2A can potentially co-regulate PAX6 in LSCs." To compare in vitro findings with in vivo results, they also generate single cell data and identify specific TFs that may play pathobiological role in disease development and progression. While the study is complete and describes well, a strong conclusion, including validation of role of some TFs such as FOSL2 through knock out experiments in model organisms or cell culture will elevate the paper more (optional). This study merits publication in high quality journal (IF:10-15)

Significance

The study is very significant not only in the context of corneal disease biology. The imbalance in interplay of TFs is often envisaged behind disease development but very few efforts of detailed analysis are undertaken. This study is performed very well and the methods are described in clear manner. Appropriate statistical methods are used where required.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

This manuscript describes studies that indicate roles for the ALK and LTK receptors in neuronal polarity, cortical patterning and behavior in mice. I really liked the study and overall think that it deserves publication in a high-ranking journal. It reports important and novel results and benefits from a comprehensive analysis at multiple levels, including cell biological, biochemical and behavior. The points raised below are suggestions for consideration at the discretion of the authors.

We thank the reviewer for the positive and enthusiastic comments on our study and especially for noting that it is appropriate for publication in a high-ranking journal. We greatly appreciate the valuable suggestions, the majority of which we have incorporated into the revised manuscript.

1. The term "DKO" appears in the Introduction without explanation. I assume this means double KO mice lacking both receptors from birth. It should be indicated here, just in case.

We have added text at the first appearance of DKO (ie results section) to indicate that this refers to double knockout mice that lack both Ltk and Alk from birth.

1. The last paragraph of the Introduction is redundant with the Abstract. This is a stylistic question, which is up to the authors. Nevertheless, as a suggestion, they could take the opportunity here to explain the rationale of the study and why they did what they did._

We have made some modifications to provide an indication of the rationale for the studies.

1. Is "single cell in situ mRNA analysis" standard in situ hybridization or something else? Why is it called "single-cell"? It could be misleading.

This was a typographical error and has been corrected to single molecule in situ.

1. In Fig. S1B, could the authors please include expression patterns of LTK in adult brain? It'd seem that is the most relevant place to look given the analysis that follows in the paper.

We have replaced the previous panels with new plots (now Fig. S1G) showing the relative expression of Ltk, Alk and their ligand, Alkal2 in embryos (E15.5), newborn (P0) and post-natal Day 2 (P2) and Day 7 (P7) and in adults both in the cortex and whole brain. The results confirm that Alk and Ltk are both expressed in the cortex and brain but in varying patterns with Alk expression decreasing with age and Ltk increasing, particularly in the cortex. In contrast, Alkal2 expression is relatively constant throughout.

Related comments #5, #7, #8 and #9.

1. I have an issue in general in the first part of the manuscript with regards to the labeling of cortical layers. How were CP, IZ and SVZ/VZ defined? Specific markers should be used to identify their actual boundaries. Guesswork from the DAPI pattern (if that is what was used) is not really appropriate.

2. In Fig. 1F, again, how were the boundaries between the cortical areas (dotted lines) determined? This is particularly important for the mutant sections....

3. In Fig. S3C-F, the all-critical quantification of Ctip2 cells at P2 seems to be missing in this figure. It would important to provide this in light of the comments above. Again, the same problem with the layer boundaries is clear here.....

4. In Figure 2A and B, % positive cells is plotted but we are not told what is the reference (100%) level. ... Also, the idea of drawing a little rectangle in the IZ and CP and counting only there is flawed. ...Finally, again, we are not told how the boundaries of the different cortex areas were established. ...

Response to related comments #5, #7, #8 and #9.

As exemplified in the related comments above, the reviewer indicated that they “__have an issue in general in the first part of the manuscript with regards to the labeling of cortical layers.”

We thank the reviewer for this insightful comment. Development of the mouse cortex follows a stereotypical pattern, thus we used a combination of DAPI ( ie nuclear density is characteristic of some layers), and layer specific markers (Satb2, Ctip2, Pax6, Sox2, Tbr2) to label the cortical layers. While this is generally acceptable for wild type mice, we agree with the reviewer’s comment that this may not be appropriate in mutant mice. Accordingly, we have now taken a more unbiased approach and repeated all of the quantitation after creating equally sized bins that span the entire cortical length and have plotted the quantitation by bin location. The general location of layers in WT mice has been marked on the images for reference. Our conclusions that there are defects in early patterning that are resolving by ~P7 is unchanged.

With this re-quantitation, some of the previous reviewer comments within #5, 7, 8 and 9 no longer apply (ie a missing plot, box placement being subjective, etc) and so have not been responded to. With regards to the question of what is the reference (ie 100%) for the plots showing the y-axis as % positive; this was determined based on the total number of DAPI+ cells counted in each region. This information has been added to the legends and methods along with details of the new quantitation method.

1. Comparing Fig. 1 and Fig. S2, there would seem to be little or no additive nor synergistic effects of the double mutation, as the phenotype in the DKO appears to be completely attributable to the Ltk KO. What does this mean? Providing the expression patterns of the two receptors at the ages used here (i.e., P2 and P7) would also be helpful.

The relative contribution of Alk or Ltk in comparison to the DKO, varies as a function of age (E15.5, P2, P7) that generally correlates with their level of expression, as per the Reviewer’s suggestion. For example, at E15.5, a reduction in the number of Sox2+ or Tbr2+ cells is observed for either Alk or Ltk knockouts alone, with a more prominent reduction in the case of Alk alone, and with the DKOs showing the greatest reduction. In contrast, when examining Ctip2 levels at P2, the loss of Ltk alone yields a stronger effect. In agreement with these observations, analysis of mRNA expression levels show that Alk levels are highest in the embryonic cortex and brain and steadily decline until adulthood, while Ltk expression increases with maximal levels occurring post-natally. As indicated for our reply to comment #4, we have now added plots showing the relative level of expression of Alk and Ltk at various ages from embryos to adults (Fig S1G).

1. At the end of page 8, it is concluded that Alk/Ltk promote neuronal migration. Is this a cell-autonomous effect? Given the very sparse expression of these receptors (Fig S1), cell-autonomy (which is being implied by the authors) is not at all clear. Is the migration of Alk+ cells affected in the Ltk mutant? Vice-versa?

In our analysis of mRNA expression using RNAscope we originally included a widefield image that depicts the entire cortex where it is difficult to see expression at the cell level. We now also provide a magnified image of the E15.5 SVZ/VZ that shows that most cells do express the receptors (Fig. S1B). Thus, the results are consistent with the idea that the defect in migration is a cell autonomous effect.

1. In Fig. S4A, as every cell in these panels bears probe signal, it'd be important to present a negative control, perhaps from KO cultures or wild type cells lacking receptor expression in the same field as expressing cells. At a 75%, 1 in 4 cells in any field should be receptor-negative.

As requested, we now provide images with a wider field of view that includes negative cells.

1. Figure S4B is difficult to interpret in the absence of Tau and MAP2 markers, as GFP does not discriminate between axons and dendrites.

In the original submission we quantitated Tau-1 and MAP2 co-stained neurons in many experiments to demonstrate that Ltk/Alk act on axons, but in some cases, we used Tuj1 to more easily visualize and quantitate neurites. Nevertheless, as requested by the reviewers, in the revised manuscript we have repeated and replaced most of the results with Tuj1 or phalloidin staining with experiments using Tau-1 and MAP2 antibodies, including Fig. 5B-D and Fig. 6A-D and G as well as for Fig. S4B. The new data is consistent with our results using Tuj1 staining and further support our conclusions that Ltk/Alk act via Igf1-r to regulate neuronal polarity.

In general, the authors are recommended to show more than one cell per condition in their figures. Readers need to be convinced that these are robust phenotypes easily observed on many cells in the same field.

Due to space constraints, we included only a single representative image for each condition and then provided quantitation to support our conclusions. We have numerous images for all of the presented data and could provide a collage for all panels if considered appropriate. In the meantime, we have added additional images for several experiments in the Main Figures (Fig. 5A-D, Fig. 6A, C) and in Suppl. Figure S4A, B, C where sufficient space was readily available.

1. In Fig. S4C and D, do the KO neurons become bipolar? I don't see examples of multipolar neurons in the images provided.

Upon siRNA mediated knockdown of Ltk and/or Alk, we observe about 50% of the neurons are bipolar (ie display the typical wild type single axon phenotype) while roughly 40% display the multiple axon phenotype. With the exception of the control (siCTL), the images provided were selected to show neurons with multiple axons. However, in some of the images, the arrowheads pointing to the axons were inadvertently omitted. These have now been added.

1. Is there a way to quantify the effects shown in Fig. 3E?

We attempted to quantitate the number and direction of neurites in the brain sections but because this is a dense tissue, even with Golgi staining, we found it impossible to trace individual neurites back to the cell body and thus were unable to quantitate the effects. As an alternative, we have provided additional images (Fig. S3B) from distinct mice to support our observations of aberrant horizontal neurites in the adult cortex.

1. The DKO display a dramatically different behavior phenotype compared to single Kos. How can this result be explained given that DKOs are indistinguishable from single KOs in all other parameters studied?

The reviewer is correct, that the single KO mice do not manifest noticeable behavioural defects except when older and challenged with the most demanding task, the Puzzle box, which measures complex executive functions. We speculate that alternative cortical re-wiring in the single knockouts is sufficient to maintain normal circuitry that cannot be compensated when both Ltk and Alk receptors are deleted. It is also possible that Ltk/Alk regulated signalling events, besides Igf-1r/PI3K could contribute to the behavioural defects observed in the DKO mice, such as the ALK-LIMK-cofilin pathway which regulates synaptic scaling mentioned by the reviewer (Zhou et al., Cell Rep. 2021). Nevertheless, the strong phenotype of the DKOs confirms that Ltk/Alk are important for proper brain function, thus our preference is to retain the behavioural data in the manuscript but to discuss that alternative Ltk/Alk pathways could contribute to the phenotype (which we have now incorporated into the text).

1. At the end of the behavior section, the authors attribute the phenotypes observed to defects in neuronal polarization. Given that polarization was only studied in vitro, it may be a premature to conclude that neurons fail to polarize in vivo in the absence of direct evidence showing this.

We agree and have modified the text to remove this inaccurate assertation.

1. Regarding P-AKT studies, it would be interesting to assess the effects of the ALK7LTK ligands (e.g., from conditioned medium) on the levels of P-AKT in WT neurons.

We agree that this would be interesting and we had attempted this experiment, but found that treatment of WT cortical neurons with medium conditioned with the ALKAL2 ligand did not change the levels of pAKT under our experimental conditions (namely 20-30 min treatment with ACM). Because the data is negative, it makes it difficult to make a firm conclusion, but if true, it is possible that other pathways might be involved when WT cortical neurons are stimulated with ligand.

1. In the mid part of page 14, the sentence "Treatment of WT cortical neurons with AG1024 at a dose (1 μM) at which only IGF-1R but not InsR was inhibited restored the single axon phenotype in DKO neurons" is confusing. Treatment performed in WT neurons but assessed in DKO neurons? This must be a typo.

Thank you for pointing out this typo. It has been corrected.

1. For completion, it would be informative to test whether IGF-1 antagonizes the effects of ALK and LTK ligands in axon formation.

As suggested, we performed the requested experiment (with 3 independent repeats). In brief, four hours post-plating neurons were treated with control or ALKAL2-conditioned media and Igf-1 was added after 1 hour. Neurons were fixed at 36 hours, stained for MAP2 and Tau-1 and axons (Tau-1+) quantitated. Consistent with our previous findings, Igf-1 promotes the formation of multiple axons while ligand inhibits axon formation. In the ligand-treated neurons, addition of Igf-1 did not result in a statistically-significant change in the number of axons. These findings are consistent with our model that activation of Ltk/Alk promotes a decrease in cell-surface Igf1-r. This data has been added to the manuscript (Fig. 7J).

1. The quality of the blot provided to illustrate levels of activated Igf-1r in Fig. 7A is clearly suboptimal. It is not apparent from that blot that phosphorylation of Igf1r is increased in the mutant neurons as the band intensities are indistinguishable. Was this performed in cortex extracts or cultured neurons? Is it affected by treatment with ALK/LTK ligands?

We apologize for a labelling error that has caused confusion for both reviewers. We have replaced the blots and corrected the labels. We have noted in the legend that the experiments were performed using cultured cortical neurons.

1. Given the physical interaction between ALK/LTK and IGF-R1, these receptors are presumably co-internalized upon ligand treatment, or? Does treatment with IGF1 induces internalization of ALK or LTK?

This is a very interesting question. Unfortunately, due to the lack of suitable antibodies for the mouse versions of Alk or Ltk, we are not able to perform these experiments in cortical neurons with endogenous receptor expression. However, our co-immunoprecipitation experiments and in vitro kinase assays, indicate that only versions of LTK and/or ALK with active kinase domains can interact with IGF-1R and that the activated LTK/ALK receptors then phosphorylate IGF-1R and trigger IGF-1R internalization (Fig. 7 and Fig. 8 model). Thus, we would expect that treatment with IGF-1 in the absence of LTK/ALK activation will not affect LTK/ALK internalization but will trigger IGF-1R endocytosis.

1. The last paragraph in the Results section may be more appropriate for Discussion to avoid repetition. But it is of course up to the authors to decide on stylistic issues.

We prefer to include a summary of the experimental findings and the model figure at the end of the results.

1. There is a discussion of possible redundancies between ALK and LTK in the Discussion section which appears to contradict itself. It is first stated (end of p. 18) that the two receptors are not redundant but both required for function. But in p. 19, the significant behavioral phenotypes observed in DKO mice, but not in single KO mice, are attributed to redundancy and compensation between the receptors. This needs some clarification. It's difficult to understand how there can be redundancy for behavior but not for structure or function.

We have clarified in the discussion, that both receptors are required in the context of neuronal polarity and migration whereas in the case of behaviour, compensatory mechanisms in neural circuitry or perhaps non-redundant Igf-1r independent pathways result in a strong phenotype only in DKO and can compensate for single but not double knockouts.

Reviewer #1 (Significance):

see above

Reviewer #2 (Evidence, reproducibility and clarity):

Christova et al. analyzed single and double knockout mice for Alk and Ltk to investigate their function in the nervous system and describe defects in cortical development and behavioral deficits. The defects in the formation of cortical layers suggest a delay in radial migration. In culture, 40% of cortical neurons from knockout embryos extend multiple axons. The mechanism responsible for this phenotype is explored in some detail. The authors conclude that Alk and Ltk function non-redundantly to regulate the Igf-1 receptor (Igf-1r). Inactivation of Alk or Ltk increases surface expression and activity of Igf-1r, which induces the formation of multiple axons. The authors propose that Alk and Ltk interact with Igf-1r and promote its endocytosis after activation by their ligand Alkal2, thereby preventing the formation of additional axons. However, the defects in neurogenesis, migration and behavior may have a different cause and should not be attributed only to Igf-1r.

We would like to thank the reviewer for all the insightful comments and suggestions which we feel have strengthened our study.

We appreciate the reviewer’s acknowledgement that we have shown that Igf-1r is in involved in Alk/Ltk-mediated regulation of axon outgrowth. To provide evidence that Igf-1r is also important for Ltk/Alk regulated migration in vivo, we explored the effect of the Igf-1r inhibitor, PPP on the migration of neurons in WT and DKO mice by BrdU labelling. Excitingly, this analysis revealed that PPP administration resulted in a partial rescue of the migration defect in Ltk/Alk DKO mice, with BrdU+ neurons being localized to the most superficial layers in P2 mice (Fig. 6F). Thus, these data are consistent with our model that loss of Ltk/Alk can disrupt both neuronal polarity and migration via IGF-1r. We do agree with the reviewer that we have not directly shown that the behavioural defects can be attributed to Igf-1r and it is certainly possible that other pathways or mechanisms may be involved in the complex phenotype. We have updated the manuscript and discuss the potential involvement of other pathways in the discussion.

Major comments<br /> 1) The role of Alk/Ltk in suppressing the formation of multiple axons is demonstrated by culturing neurons from knockout mice, suppression with siRNAs and treatment with inhibitors. These experiments consistently show that about 40% of cultured neurons extend more than one axon when Alk, Ltk or both are inactivated. Single and double knockout mice are largely normal with the exception of a delay in the formation of distinct cortical layers. The phenotypes of the knockout lines indicate a function in cortical development but Alk and Ltk are not "indispensable" as suggested (p. 18)._

We will modify the wording to remove the statement that Alk and Ltk are “indispensable” for cortical patterning and rather will indicate that the receptors ‘contribute’ to the timing of cortical patterning.

The morphology of cortical neurons was analyzed by Golgi staining. A few potential axons (Fig. 3E) were identified only by an absence of dendritic spines and their aberrant trajectory. These results indicate that there are ectopic extensions in the cortex but do not demonstrate that neurons extend multiple axons also in vivo. It has to be confirmed that these extensions are positive for axon-specific markers and that several axons originate from one soma to demonstrate a multiple axon phenotype in vivo. A quantification of the number of neurons with multiple axons would be required to conclude that this phenotype occurs at a similar frequency in vivo.

As indicated in response to reviewer #1, we attempted to quantitate the Golgi stained images but found it impossible to trace individual neurites to the cell body and thus could not unambiguously identify and quantitate axons. Accordingly, and as suggested by the reviewer, we have modified our conclusion to simply state there are aberrant extensions in the cortex in vivo. Although we were unable to do quantitation, to further support our conclusions, we have provided additional Golgi stained images of WT and DKO mice from an independent experiment (Fig. S3B).

2) According to the model presented in Fig. 7, Alkal2 activates Alk and Ltk, which stimulate the endocytosis of Igf-1r and thereby prevents the formation of additional axons. A quantification of Igf-1r surface levels by the biotinylation of surface proteins and Western blot shows an increase in knockout neurons. The authors suggest that Alk/Ltk activation stimulates Igf-1r endocytosis but do not demonstrate this directly. An increase in surface expression could also result from a stimulation of exocytosis or recycling.

We showed that ligand-induced activation of Ltk/Alk in WT neurons resulted in a loss of biotin-labelled cell-surface Igf-1r, which is strongly indicative of increased internalization and cannot be explained by exocytosis. However, the reviewer is correct, that we cannot exclude the possibility that changes in exocytosis or recycling might also occur and that in the unstimulated DKO neurons, the increase in surface expression of Igf-1r could also result from a stimulation of exocytosis or recycling. Indeed, several papers (Laurino et al, 2005, PMID: 16046480; Oksdath et al, 2017, PMID: 27699600; Quiroga et al, 2018, PMID: 29090510) have reported that exocytosis mediated transport of IGF-1R and activation of IGF-1R/PI3K pathway is essential for the regulation of membrane expansion during axon formation. Accordingly, we have modified the discussion text to incorporate this possibility.

3) The localization of Alk, Ltk and Alkal2 was determined by in situ hybridization. The signals are weak and it is not clear if they are specific because a negative control is missing. An analysis by immunofluorescence staining would be more informative.

RNAscope is designed so that a single molecule of RNA is visualized as a punctuate signal dot with high specificity. In lower magnification images, such as those we showed to provide an overall view of expression in the cortex, it is difficult to discern the individual ‘dots’, particularly for genes with low expression, giving the impression that the signal is weak. However, at high magnification (63X) the signals are readily visible as seen in a new panel in Fig. S1B). We also neglected to mention that positive probes with all 3 labels (POLR2A: Channel C1, PPIB: Channel C2, UBC:Channel C3) as well as a negative probe (Bacterial dap gene) supplied by the manufacturer were used on our samples to validate specificity. We have corrected the oversight and have now added this information to the methods section.

Regarding immunofluorescence, we have rigorously tested numerous commercially-available antibodies and have undertaken repeated attempts to produce our own antibodies that recognize mouse Ltk or Alk, and are appropriate for immunofluorescence, but have had no success. The high specificity enabled by the RNAscope technology is thus currently the most reliable way we can examine expression, with the added advantage that we can simultaneously assess expression of both receptors and the ligand in an individual cell within a section.

Alk appears to be expressed mainly in the ventricular zone (VZ) while Ltk shows a low expression in the SVZ and the cortical plate (CP). This expression pattern is not consistent with a function in regulating axon formation in multipolar neurons, which extend axons in the lower intermediate zone (IZ) (Namba et al., Neuron 2014) and not in the VZ or SVZ (p. 18).

It is well described that multipolar neurons can be found in the SVZ, while bipolar neurons are preferentially in the IZ. Neurons expressing Ltk, Alk and their ligand, Alkal2 can be found in both compartments (albeit levels appear higher in the SVZ), thus we feel our results are consistent with a role for the receptors in regulating neuronal polarization.

It is also essential to analyze the subcellular localization of Alk and Ltk at least in cultured neurons. Ltk has been reported as an ER-resident protein that regulates the export from the ER (Centonze et al., 2019), which would not be consistent with the model.

Unfortunately, the lack of antibodies with mouse reactivity prevents us from analyzing the subcellular localization of Alk and Ltk in cultured neurons. As mentioned by the reviewer, LTK has been reported as an ER-resident protein (in cancer cells) and similarly, many other tyrosine kinase receptors including IGF1R, have been reported to be localized to diverse intracellular compartments like Golgi, nucleus or mitochondria (reviewed in Rieger and O’Connor, 2021, Front Endocrinol:PMID: 33584548). However, since extracellular ligands for LTK and ALK are known, we feel it is a reasonable expectation that they will have a role as cell-surface receptors. Understanding the functions of RTK receptors and the interplay between the various compartments would nevertheless be an interesting area for future research.

4) The results convincingly show that an increased activity of Igf-1r is responsible for the formation of additional axons by cultured knockout neurons. The model in Fig. 7 explains how Alk/Ltk suppress the formation of multiple axons in culture but a key question remains to be addressed: why does Igf-1r remain active in the future axon? Are Alk/Ltk restricted to or selectively activated in dendrites? It is important to determine if Alk and Ltk are absent from the future axon before or after neuronal polarity is established.

We thank the reviewer for acknowledging that we have provided convincing data that increased activity of Igf-1r is responsible for the formation of multiple axons. Addressing why Igf-1r remains active in the future axon and if and how Ltk/Alk are selectively activated in dendrites and axons are all excellent questions, which we plan to pursue in future work, particularly when antibodies for Alk and Ltk become available.

Which cells produce Alkal2 in neuronal cultures and in vivo?_ _These points can be easily addressed and should be investigated.

We have confirmed that Alkal2 is expressed in the isolated cortical neurons, consistent with our demonstration that siRNA-mediated abrogation of Alkal2 expression in cultured neurons regulates polarity and that ligand levels do not change in Ltk/Alk double knock out mice (Fig. S1G and S6A). Whether other non-neuronal cell types also express Alkal2 would be an interesting future direction.

Why does an increase of Igf-1r surface expression in knockout neurons result in a stimulation of Igf-1r autophosphorylation? Neurons are cultured in a defined medium without Igf-1 and increased surface levels by themselves should not lead to an increased activity.

We have not mechanistically determined why/how Igf-1r displays enhanced autophosphorylation in DKO neurons. Thus, we can only speculate about possibilities. Perhaps there are low levels of Igf-1 in the cortical cell extracts, or is produced by the cortical neurons; there may be compensatory mechanisms engaged when Ltk/Alk are lost to ensure neuronal survival, or perhaps the increase in cell-surface Igf-1r promotes ligand-independent activation of receptors in the absence of ligand.

The results presented in this manuscript are consistent with a role of Igf-1r in the formation of multiple axons in the absence of Alk/Ltk. However, inhibition of Igf-1r by various means does not prevent axon formation in controls. Igf-1 has been implicated in axon formation (Sosa at al., 2006) but a knockout of Igf-1r does not result in a loss of axons but a reduction of axon length in cultured neurons (Jin et al., PLoS One 2019). Axon-specific markers are used only for some experiments but not in Figs. 3D, 5B-D and 6 where the neuronal marker Tuj1 does not allow the unambiguous identification of axons. Staining with an axonal marker and a quantification of axon length are required to distinguish between a block in axon formation and a reduction in axon growth in Figs. 3A, 5 and 6.

In the original submission we quantitated Tau-1 and MAP2 co-stained neurons in many experiments to demonstrate that Ltk/Alk act on axons, but in some cases we used Tuj1 to more easily visualize and quantitate neurites. Nevertheless, as requested by the reviewers, in the revised manuscript we have repeated and replaced most of the results with Tuj1 or phalloidin staining with experiments using Tau-1 and MAP2 antibodies, including Fig. 5B-D and Fig. 6A-D and G, as well as for Fig. S4B requested by reviewer #1). The new data is consistent with our results using Tuj1 staining and further support our conclusions that Ltk/Alk act via Igf1-r to regulate neuronal polarity. With regards to Fig. 3D, we have been experiencing ongoing technical issues in generating human stem cell derived cortical neurons and have been unable to undertake Tau1/MAP2 staining of the human cortical neurons. Given that the point being made is minor, we have removed this panel from the paper.

With regards to the comment on that inhibition of Igf1-r did not prevent basal axon formation: in our prior quantitation of WT neurons in which Igf1-r was inhibited using either siIgf1-r or PPP, we noticed a trend towards an increase in the number of neurons with no axons, but this was not statistically significant. Upon the repeat of experiments and re-quantitation with Tau-1/MAP2 co-staining, we do see a statistically-significant increase in the number of WT neurons without axons. This is in agreement with several prior studies (including one cited by the reviewer) indicating Igf1-r is important for neuronal polarity (Sosa, 2006; PMID:16845384, Neito Guil 2017 PMID:28794445). The text has been modified accordingly.

5) The analysis with layer specific markers and BrdU labeling reveals defects in the formation of cortical layers that suggest a delay in neuronal migration. The number of Sox2+ and Tbr2+ cells is lower in knockout neurons indicating a possible reduction in the number of proliferating progenitors and a defect in neurogenesis (Fig. 1). The number of neurons positive for layer-specific markers or BrdU was quantified as the percent of DAPI-positive cells. This does not allow distinguishing between a change in the distribution and a reduction in the number of neurons due to defects in neurogenesis. It would be more informative to quantify the total number Ctip+, Satb2+ or BrdU+ cells in the VZ, SVZ, IZ and CP._

In the in vivo BrdU labelling experiment, we did not co-stain sections with DAPI. However, in the immunofluorescence analysis in mice of the same ages, we did determine the total number of cells (ie by DAPI) that is shown in the plots in Fig. 1A and Fig. S2A/B. These results show that there are a similar number of cells in WT and mutant SVZ/VZ, consistent with the notion that there is a change in distribution rather than in reduction in the number of neurons due to defective neurogenesis. We neglected to mention this important point in the results and have now modified the text accordingly.

6) The deficits observed in behavioral tests do not correlate with the defects in neuronal development. While the single knockouts show defects in cortical development only the double knockout displays behavioral deficits. The behavioral phenotype could be completely independent of Igf-1r. Alk has been implicated in regulating retrograde transport (Fellows et al., EMBO Rep. 2020) and synaptic scaling (Zhou et al., Cell Rep. 2021). Since there is no clear correlation between structural and behavioral changes these data are not obviously linked to the other results.

The reviewer is correct, that the single KO mice do not manifest noticeable behavioural defects except when older and challenged with the most demanding task, the Puzzle box, which measures complex executive functions. We speculate that alternative cortical re-wiring in the single knockouts is sufficient to maintain normal circuitry that cannot be compensated when both Ltk and Alk receptors are deleted. However, we do agree that Ltk/Alk regulated signalling events, besides Igf-1r/PI3K could contribute to the behavioural defects observed in the DKO mice, such as the ALK-LIMK-cofilin pathway which regulates synaptic scaling as cited by the reviewer (Zhou et al., Cell Rep. 2021). Nevertheless, the strong phenotype of the DKOs confirms that Ltk/Alk are important for proper brain function, thus our preference is to retain the behavioural data in the manuscript but to discuss that alternative Ltk/Alk pathways could contribute to the phenotype (which we have now incorporated into the text).

It should be noted that the study by Fellows et al in EMBO Rep 2020 shows Igf1-r, not ALK regulates retrograde transport so we have not included this study in the updated text.

Minor comments

1) Fig. 3 shows defects in the corpus callosum where axons are restricted to the upper half in the wild type but not the knockout. These results could indicate a guidance defect but do not show a "failure in axon migration through the corpus callosum" (p. 17). It is also not demonstrated "that the aberrant axon tracts may be the result of effects on neuronal morphology" (p. 19). Without additional experiments to trace axonal projections e.g. by DiI labeling it is not possible to determine the actual cause for the observation shown in Fig. 3F._

We agree with the reviewer and have modified the concluding sentence so that the defects are described without attributing the cause to the defects on neuronal morphology.

2) Active kinases from SignalChem are used for the in vitro kinase assays. The increased phosphorylation of Igf-1r could also result from a stimulation of auto-phosphorylation and not a direct phosphorylation by Ltk. Previous results indicate that phosphorylation of Y1250/1251 leads to increased internalization and degradation (Rieger et al., Sci. Signal. 2020), which would be an alternative explanation how Alk/Ltk regulate surface expression. Antibodies that are specific for Igf-1r phosphorylation at Y1135/1136 or Y1250/1251 could address this possibility (Rieger at al., Sci. Signal. 2020).

It is rather surprising that for the Igf-1r, which is such a well-studied receptor, the mechanisms that regulate trafficking, exocytosis recycling, etc are so poorly understood and that this topic is currently an active area of investigation. The focus of our study was on understanding the role of Ltk/Alk in the brain and as part of this effort we demonstrated that Ltk/Alk can control neuronal polarity through Igf-1r phosphorylation. We believe that shedding light on the detailed mechanism of how enhanced Igf-1r phosphorylation induced by Ltk/Alk activation regulates Igf-1r trafficking is an exciting project for future work, but we feel that to thoroughly investigate this question is beyond the scope of the current study. We have, nevertheless, highlighted these points with additional references in the discussion.

3) The specificity of the siRNAs has to be verified in neurons by rescue experiments and the suppression of the targeted proteins confirmed by immunofluorescence staining.

We agree that rescue experiments are the gold standard, and we attempted to do this. However, we found that nucleofection of both siRNAs and cDNAs encoding either EGFP alone or Ltk/Alk was highly toxic to neurons with few surviving the treatment. As an alternative we used a pool of siRNAs, to minimize off-target effects and used genetic KOs or chemical inhibitors to verify the observations.

4) The position of molecular weight markers is missing for most Western blots.

We added the position of molecular weight markers for all the western blots in the revised manuscript.

5) It is not indicated which conditions show a significant difference in Fig. 6.

We thank the reviewer for pointing this out. We added the significant differences to all figures, including Fig. 6.

6) Why does the Western blot in Fig. 7A show a double band with the anti-phospho-Igf-1r antibody in the knockout? Which of the bands was used for the quantification?

We apologize for a labelling error that has caused confusion for both reviewers. We have replaced the blots and corrected the labels.

7) Details of the plasmids used and information (catalog number) for recombinant GST-Ltk and His-Igf-1r should be included in Materials and Methods.

The additional information and catalog numbers have been added to the Materials and Methods.

Reviewer #2 (Significance):

The receptor tyrosine kinase Alk has been studied mainly for its involvement in several types of cancer but the physiological functions of Alk and its close relative Ltk remain poorly understood. The regulation of Igf-1r is an interesting and important result to understand the physiological function of Alk and Ltk. However, several points have to be addressed before the manuscript would be suitable for publication.

We thank the reviewer for indicating that this is interesting and important study. We trust that the additional data and clarifications provided, have addressed the reviewers concerns.

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

Christova et al. analyzed single and double knockout mice for Alk and Ltk to investigate their function in the nervous system and describe defects in cortical development and behavioral deficits. The defects in the formation of cortical layers suggest a delay in radial migration. In culture, 40% of cortical neurons from knockout embryos extend multiple axons. The mechanism responsible for this phenotype is explored in some detail. The authors conclude that Alk and Ltk function non-redundantly to regulate the Igf-1 receptor (Igf-1r). Inactivation of Alk or Ltk increases surface expression and activity of Igf-1r, which induces the formation of multiple axons. The authors propose that Alk and Ltk interact with Igf-1r and promote its endocytosis after activation by their ligand Alkal2, thereby preventing the formation of additional axons. However, the defects in neurogenesis, migration and behavior may have a different cause and should not be attributed only to Igf-1r.

Major comments

1. The role of Alk/Ltk in suppressing the formation of multiple axons is demonstrated by culturing neurons from knockout mice, suppression with siRNAs and treatment with inhibitors. These experiments consistently show that about 40% of cultured neurons extend more than one axon when Alk, Ltk or both are inactivated. Single and double knockout mice are largely normal with the exception of a delay in the formation of distinct cortical layers. The phenotypes of the knockout lines indicate a function in cortical development but Alk and Ltk are not "indispensable" as suggested (p. 18). The morphology of cortical neurons was analyzed by Golgi staining. A few potential axons (Fig. 3E) were identified only by an absence of dendritic spines and their aberrant trajectory. These results indicate that there are ectopic extensions in the cortex but do not demonstrate that neurons extend multiple axons also in vivo. It has to be confirmed that these extensions are positive for axon-specific markers and that several axons originate from one soma to demonstrate a multiple axon phenotype in vivo. A quantification of the number of neurons with multiple axons would be required to conclude that this phenotype occurs at a similar frequency in vivo.
2. According to the model presented in Fig. 7, Alkal2 activates Alk and Ltk, which stimulate the endocytosis of Igf-1r and thereby prevents the formation of additional axons. A quantification of Igf-1r surface levels by the biotinylation of surface proteins and Western blot shows an increase in knockout neurons. The authors suggest that Alk/Ltk activation stimulates Igf-1r endocytosis but do not demonstrate this directly. An increase in surface expression could also result from a stimulation of exocytosis or recycling.
3. The localization of Alk, Ltk and Alkal2 was determined by in situ hybridization. The signals are weak and it is not clear if they are specific because a negative control is missing. An analysis by immunofluorescence staining would be more informative. Alk appears to be expressed mainly in the ventricular zone (VZ) while Ltk shows a low expression in the SVZ and the cortical plate (CP). This expression pattern is not consistent with a function in regulating axon formation in multipolar neurons, which extend axons in the lower intermediate zone (IZ) (Namba et al., Neuron 2014) and not in the VZ or SVZ (p. 18).<br /> It is also essential to analyze the subcellular localization of Alk and Ltk at least in cultured neurons. Ltk has been reported as an ER-resident protein that regulates the export from the ER (Centonze et al., 2019), which would not be consistent with the model.
4. The results convincingly show that an increased activity of Igf-1r is responsible for the formation of additional axons by cultured knockout neurons. The model in Fig. 7 explains how Alk/Ltk suppress the formation of multiple axons in culture but a key question remains to be addressed: why does Igf-1r remain active in the future axon? Are Alk/Ltk restricted to or selectively activated in dendrites? Which cells produce Alkal2 in neuronal cultures and in vivo? These points can be easily addressed and should be investigated. It is important to determine if Alk and Ltk are absent from the future axon before or after neuronal polarity is established. Why does an increase of Igf-1r surface expression in knockout neurons result in a stimulation of Igf-1r autophosphorylation? Neurons are cultured in a defined medium without Igf-1 and increased surface levels by themselves should not lead to an increased activity.<br /> The results presented in this manuscript are consistent with a role of Igf-1r in the formation of multiple axons in the absence of Alk/Ltk. However, inhibition of Igf-1r by various means does not prevent axon formation in controls. Igf-1 has been implicated in axon formation (Sosa at al., 2006) but a knockout of Igf-1r does not result in a loss of axons but a reduction of axon length in cultured neurons (Jin et al., PLoS One 2019). Axon-specific markers are used only for some experiments but not in Figs. 3D, 5B-D and 6 where the neuronal marker Tuj1 does not allow the unambiguous identification of axons. Staining with an axonal marker and a quantification of axon length are required to distinguish between a block in axon formation and a reduction in axon growth in Figs. 3A, 5 and 6.
5. The analysis with layer specific markers and BrdU labeling reveals defects in the formation of cortical layers that suggest a delay in neuronal migration. The number of Sox2+ and Tbr2+ cells is lower in knockout neurons indicating a possible reduction in the number of proliferating progenitors and a defect in neurogenesis (Fig. 1). The number of neurons positive for layer-specific markers or BrdU was quantified as the percent of DAPI-positive cells. This does not allow distinguishing between a change in the distribution and a reduction in the number of neurons due to defects in neurogenesis. It would be more informative to quantify the total number Ctip+, Satb2+ or BrdU+ cells in the VZ, SVZ, IZ and CP.
6. The deficits observed in behavioral tests do not correlate with the defects in neuronal development. While the single knockouts show defects in cortical development only the double knockout displays behavioral deficits. The behavioral phenotype could be completely independent of Igf-1r. Alk has been implicated in regulating retrograde transport (Fellows et al., EMBO Rep. 2020) and synaptic scaling (Zhou et al., Cell Rep. 2021). Since there is no clear correlation between structural and behavioral changes these data are not obviously linked to the other results.

Minor comments

1. Fig. 3 shows defects in the corpus callosum where axons are restricted to the upper half in the wild type but not the knockout. These results could indicate a guidance defect but do not show a "failure in axon migration through the corpus callosum" (p. 17). It is also not demonstrated "that the aberrant axon tracts may be the result of effects on neuronal morphology" (p. 19). Without additional experiments to trace axonal projections e.g. by DiI labeling it is not possible to determine the actual cause for the observation shown in Fig. 3F.
2. Active kinases from SignalChem are used for the in vitro kinase assays. The increased phosphorylation of Igf-1r could also result from a stimulation of auto-phosphorylation and not a direct phosphorylation by Ltk. Previous results indicate that phosphorylation of Y1250/1251 leads to increased internalization and degradation (Rieger et al., Sci. Signal. 2020), which would be an alternative explanation how Alk/Ltk regulate surface expression. Antibodies that are specific for Igf-1r phosphorylation at Y1135/1136 or Y1250/1251 could address this possibility (Rieger at al., Sci. Signal. 2020).
3. The specificity of the siRNAs has to be verified in neurons by rescue experiments and the suppression of the targeted proteins confirmed by immunofluorescence staining.
4. The position of molecular weight markers is missing for most Western blots.
5. It is not indicated which conditions show a significant difference in Fig. 6.
6. Why does the Western blot in Fig. 7A show a double band with the anti-phospho-Igf-1r antibody in the knockout? Which of the bands was used for the quantification?
7. Details of the plasmids used and information (catalog number) for recombinant GST-Ltk and His-Igf-1r should be included in Materials and Methods.

Significance

The receptor tyrosine kinase Alk has been studied mainly for its involvement in several types of cancer but the physiological functions of Alk and its close relative Ltk remain poorly understood. The regulation of Igf-1r is an interesting and important result to understand the physiological function of Alk and Ltk. However, several points have to be addressed before the manuscript would be suitable for publication.

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Referee #1

Evidence, reproducibility and clarity

This manuscript describes studies that indicate roles for the ALK and LTK receptors in neuronal polarity, cortical patterning and behavior in mice. I really liked the study and overall think that it deserves publication in a high-ranking journal. It reports important and novel results and benefits from a comprehensive analysis at multiple levels, including cell biological, biochemical and behavior. The points raised below are suggestions for consideration at the discretion of the authors.

1. The term "DKO" appears in the Introduction without explanation. I assume this means double KO mice lacking both receptors from birth. It should be indicated here, just in case.
2. The last paragraph of the Introduction is redundant with the Abstract. This is a stylistic question, which is up to the authors. Nevertheless, as a suggestion, they could take the opportunity here to explain the rationale of the study and why they did what they did.
3. Is "single cell in situ mRNA analysis" standard in situ hybridization or something else? Why is it called "single-cell"? It could be misleading.
4. In Fig. S1B, could the authors please include expression patterns of LTK in adult brain? It'd seem that is the most relevant place to look given the analysis that follows in the paper.
5. I have an issue in general in the first part of the manuscript with regards to the labeling of cortical layers. How were CP, IZ and SVZ/VZ defined? Specific markers should be used to identify their actual boundaries. Guesswork from the DAPI pattern (if that is what was used) is not really appropriate.
6. Comparing Fig. 1 and Fig. S2, there would seem to be little or no additive nor synergistic effects of the double mutation, as the phenotype in the DKO appears to be completely attributable to the Ltk KO. What does this mean? Providing the expression patterns of the two receptors at the ages used here (i.e., P2 and P7) would also be helpful.
7. In Fig. 1F, again, how were the boundaries between the cortical areas (dotted lines) determined? This is particularly important for the mutant sections, as apparent cortical thickness would be easily be affected by the plane of the section. Simply assuming that the CP is of equal thickness than the one in the WT may be incorrect. I feel the authors cannot just place dotted lines in the figure without explaining the criteria that was used to determine their location. Also, there is a significant (many fold) increase in Ctip2 cells in the IZb of the mutant (1F) that it's not explained in the text. The quantification of Ctip2 cells in the CP and IZa of the mutant is missing in the histogram. It should be indicated, even if very low. Again, the key point here is the criteria used for the<br /> boundaries between areas. May be what it's marked as IZa in the mutant is still part of the CP, in which case the number of Ctip2 cells would be increased there, not decreased, as claimed in the text.
8. In Fig. S3C-F, the all-critical quantification of Ctip2 cells at P2 seems to be missing in this figure. It would important to provide this in light of the comments above. Again, the same problem with the layer boundaries is clear here. The Ltk KO would have normal levels of Ctip2 cells if the CP thickness were to be larger (due to e.g., the plane of the section not being perfectly perpendicular to the brain surface).
9. In Figure 2A and B, % positive cells is plotted but we are not told what is the reference (100%) level. Was it the total number of cells in the entire cortex (including SVZ and VZ)? That cannot be the case, since CP+IZ in WT alone reaches almost 100%. What is 100% here please? Also, the idea of drawing a little rectangle in the IZ and CP and counting only there is flawed. The values would change drastically depending on where the rectangle is placed. They need to count the whole field of view, as it was done in the previous figures. Finally, again, we are not told how the boundaries of the different cortex areas were established. As explained earlier, distance from the surface (or from<br /> the bottom) of the cortex would be greatly affected by the plane of the section. This problem will need a more satisfying solution for the data to be interpreted in the way it has been done.
10. At the end of page 8, it is concluded that Alk/Ltk promote neuronal migration. Is this a cell-autonomous effect? Given the very sparse expression of these receptors (Fig S1), cell-autonomy (which is being implied by the authors) is not at all clear. Is the migration of Alk+ cells affected in the Ltk mutant? Vice-versa?
11. In Fig. S4A, as every cell in these panels bears probe signal, it'd be important to present a negative control, perhaps from KO cultures or wild type cells lacking receptor expression in the same field as expressing cells. At a 75%, 1 in 4 cells in any field should be receptor-negative.
12. Figure S4B is difficult to interpret in the absence of Tau and MAP2 markers, as GFP does not discriminate between axons and dendrites. In general, the authors are recommended to show more than one cell per condition in their figures. Readers need to be convinced that these are robust phenotypes easily observed on many cells in the same field.
13. In Fig. S4C and D, do the KO neurons become bipolar? I don't see examples of multipolar neurons in the images provided.
14. Is there a way to quantify the effects shown in Fig. 3E?
15. The DKO display a dramatically different behavior phenotype compared to single Kos. How can this result be explained given that DKOs are indistinguishable from single KOs in all other parameters studied?
16. At the end of the behavior section, the authors attribute the phenotypes observed to defects in neuronal polarization. Given that polarization was only studied in vitro, it may be a premature to conclude that neurons fail to polarize in vivo in the absence of direct evidence showing this.
17. Regarding P-AKT studies, it would be interesting to assess the effects of the ALK7LTK ligands (e.g., from conditioned medium) on the levels of P-AKT in WT neurons.
18. In the mid part of page 14, the sentence "Treatment of WT cortical neurons with AG1024 at a dose (1 μM) at which only IGF-1R but not InsR was inhibited restored the single axon phenotype in DKO neurons" is confusing. Treatment performed in WT neurons but assessed in DKO neurons? This must be a typo.
19. For completion, it would be informative to test whether IGF-1 antagonizes the effects of ALK and LTK ligands in axon formation.
20. The quality of the blot provided to illustrate levels of activated Igf-1r in Fig. 7A is clearly suboptimal. It is not apparent from that blot that phosphorylation of Igf1r is increased in the mutant neurons as the band intensities are indistinguishable. Was this performed in cortex extracts or cultured neurons? Is it affected by treatment with ALK/LTK ligands?
21. Given the physical interaction between ALK/LTK and IGF-R1, these receptors are presumably co-internalized upon ligand treatment, or? Does treatment with IGF1 induces internalization of ALK or LTK?
22. The last paragraph in the Results section may be more appropriate for Discussion to avoid repetition. But it is of course up to the authors to decide on stylistic issues.
23. There is a discussion of possible redundancies between ALK and LTK in the Discussion section which appears to contradict itself. It is first stated (end of p. 18) that the two receptors are not redundant but both required for function. But in p. 19, the significant behavioral phenotypes observed in DKO mice, but not in single KO mice, are attributed to redundancy and compensation between the receptors. This needs some clarification. It's difficult to understand how there can be redundancy for behavior but not for structure or function.

Significance

see above

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

The manuscript from Li et al. describes the authors' attempt to redirect the exocytic Rab Sec4 to endocytic vesicles by fusing the GEF-domain of Sec2 to the CUE domain of the endosomal GEF Vps9, which binds to ubiquitin. The authors show that the localization of the Sec2GEF-GFP-CUE construct is slightly shifted from polarized towards non-polarized sites. Sec2GFP-CUE positive structures acquire Sec4 and Sec4 effectors like exocytic vesicles but are less motile and show delayed plasma membrane fusion. Expression of Sec2GEF-GFP-CUE was enhanced if expressed in a subset of secretory and endocytic mutants and cause delayed Mup1 uptake from the plasma membrane. As Vps9, Sec2GEF-GFP-CUE accumulated on Class E compartments in vps4Δ strains.<br /> The authors ask here whether vesicular identity is largely predetermined by the correct localization of the specific GEFs of small GTPases and thus localization of the Rab. Although this an interesting hypothesis, the authors observed that endocytic traffic was not reversed by relocating Sec4 to these vesicles. This seems to be due to the strong affinity of the Sec2 GEF-domain for Sec4 but probably also due to the rather weak relocalization via the CUE domain. Thus, only a portion of Sec2 was displaced from its native site. Since the efficiency of this rewiring was not defined, it remains unclear whether the observed mild effects indeed speak against the assumed dominant role of the GEFs and small GTPases in shaping organelle identity or whether they are rather due to an inefficient relocalization.

Our data demonstrate a dramatic relocalization of Sec2-GEF-GFP-CUE relative to Sec2-GEF-GFP. In the case of Sec2-GEF-GFP or Sec2-GEF-GFP-CUE M419D the cytoplasmic pool is predominant and only 30% of cells exhibit a detectable concentration, while in the case of Sec2-GEF-GFP-CUE 80% of cells show bright puncta and there is little or no detectable cytoplasmic pool (Fig 1A). Clearly the CUE domain can function as a localization domain that relies upon ubiquitin binding. Furthermore, half of the Sec2-GEF-GFP-CUE puncta colocalize with Vps9 (Fig S1). The high cytoplasmic background of Vps9 could mask additional colocalization, therefore we reexamined colocalization in a vps4__D_ _mutant in which the Vps9 cytoplasmic pool is reduced due to increased association with the expanded Class E late endosomes. In this situation we observe about 80% colocalization with Vps9 as well as substantial colocalization with Ypt51 and Vps8 (Fig 2). We now also show significant colocalization with PI(3)P (Fig S3D). Thus, our data demonstrate that addition of the CUE domain does indeed relocalize Sec2GEF to endocytic membranes. The Sec2 GEF activity then leads to the recruitment of Sec4 and Sec4 effectors, including Myo2 which in turn leads to their delivery to polarized sites. We now show by EM that the bright Sec2-GEF-GFP-CUE puncta correlate with clusters of 80 nm vesicles (Fig 5B). Our data argues that these are hybrid compartments carrying both endocytic and exocytic markers. We have restructured our paper to help clarify and emphasize this key point.

Specific comments:<br /> 1. The authors state decidedly that the recruitment of Vps9 occurs ubiquitin-dependent via the CUE-domain. While the CUE-domain is the only known and a likely localization determinant of Vps9, it was not a strong localization determinant. Apart from being present in some puncta, Vps9 localized strongly to the cytosol (Paulsel et al. 2013, Nagano et al. 2019). Shideler et al. also showed that ubiquitin-binding is not required for Vps9 function in vivo, which indicates that other localizing mechanisms may play a role e. g. by positive feedback of GEF-domain-Rab5 interactions which might be initiated by the other Rab5-GEF Muk1 or as suggested by transport from the Golgi (Nagano et al. 2019). These observations indicate that the CUE-domain is a rather weak recruitment domain, which was not discussed in this manuscript. The localization of the Sec2GEF-GFP-control to the polarized sites in 30% of the cells furthermore suggests that the used Sec2GEF-GFP-CUE retains some native localization via the GEF-domain. Since the relocation efficiency of Sec2GEF-GFP-CUE was not defined, the obtained phenotypic effects allow for only vague conclusions. Although the mild endo- and exocytosis defects as well as the accumulation of Sec2GEF-GFP-CUE at Class E compartments indicate that the CUE-domain indeed conferred some relocation to endosomes, this was not shown for the sec2Δ strain e. g. by looking at colocalizations with endocytic versus exocytic markers and comparing their relative abundance at the Sec2GEF-GFP-CUE-positive structures. While some of the Sec2GEF-GFP-CUE-positive structures colocalized with Mup1 in the Mup1-uptake assay, it would be important to clarify how many endosomal properties are retained and how many exocytic properties are gained by these chimeric vesicles e. g. by looking for the presence of specific phosphoinositides, or Rab5 and Rab5 effectors. A competition between endosomal and the acquired exocytic factors could also be another possible explanation for the immobility of the Sec2GEF-GFP-CUE structures and less efficient recruitment of Sec4 effectors in addition to the proposed lack of PI4P.

As summarized above, we observed dramatic relocalization of Sec2GEF that was strongly dependent upon the ability of the CUE domain to bind to ubiquitin. We also observed colocalization with Ypt51 and Vps8 as well as transient colocalization with internalized Mup1. We now also show significant colocalization with PI(3)P (Fig S3D). Full length Vps9 is probably subject to additional levels of regulation, perhaps autoinhibitory in nature, however our construct contains only the CUE domain which can clearly function as an efficient localization domain on its own. The high cytoplasmic pool of Vps9 reflects the rapid turnover of its ubiquitin binding sites, since it is efficiently recruited to membranes in vps4__D_ cells. The relocalized Sec2GEF domain was quite effective in recruiting Sec4 as well as most known Sec4 effectors. The recruitment of Myo2 leads to localization to sites of polarized growth. All of our studies were done in a sec2__D _background except for the analysis of dominant growth effects, as now explicitly stated at the beginning of the Results section.

1. While the colocalization of the Sec2GEF-GFP-CUE-signal with Sec4 indicates that this GEF-construct is generally active, it remains unclear whether the activity of the tagged constructs differ from that of the wild type Sec2 protein. This could be analyzed in vitro via a MANT-GDP GEF-activity assay (Nordmann et al., 2010). Again, it remains unclear how much of the Sec2GEF-Sec4 colocalization represents the retained native localization versus synthetic localization at chimeric endo-exocytic vesicles.

The structure and nucleotide exchange mechanism of the Sec2 GEF domain have been thoroughly analyzed in prior studies and are well understood. There is no reason to think that the constructs we generated here would alter the exchange activity as the fusions are far removed from the Sec4 binding site and our analysis here confirms that they are active in vivo. We do not feel that there would be much to be gained by doing in vitro exchange assays and it would entail a great deal of work.

1. The authors mention that tagging with GFP increases the stability of the expressed constructs. However, it remains unclear whether this is also the case for the other tags (NeonGreen, mCherry) used in the other experiments. Are the constructs expressed at similar levels?

We have compared the levels of the various tagged constructs and they appear to be similar (Fig S5A).

1. In Figure 5: The incomplete colocalization of Sec2GEF-GFP-CUE with Vps9 is explained by the short-timed accessibility of ubiquitin moieties. Apart from the likely retained native localization or weak CUE-domain-function, this observation could also be due to competition between Vps9 and Sec2GEF-GFP-CUE for the available ubiquitin target structures.

As previously shown, Vps9 normally displays a prominent cytoplasmic pool. Deletion of Vps4 leads to recruitment of this pool to expanded endosomes through an increase in the lifetime of the ubiquitin binding sites. The high cytoplasmic background in VPS4 cells could obscure some colocalization with Sec2GEF-GFP-CUE and indeed we observe increased colocalization in vps4__D_ _cells in which the cytoplasmic pool of Vps9 has been recruited to endosomes. Expression of Sec2GEF-GFP-CUE does not appear to significantly alter the localization of Vps9.

Minor remarks:<br /> 1. Fig. 3C do not contain the arrowheads as indicated in the legend, making it harder to interpret.

These have been added.

1. The image chosen for Sec2-GFP in Fig. 4B suggests less colocalization between Sec2-GFP and Sec8 than between Sec2GEF-GFP-CUE and Sec8. They rather look next to each other.

The images initially chosen were not representative. We have replaced them with better images from the same experiment.

1. Figure 5: While resolution limits are possibly reached regarding endosomes, it might be interesting to check by thin section electron microscopy whether and how class E compartment formation is affected by Sec2GEF-GFP-CUE expression.

We have now done EM using permanganate fixation of both VPS4 and vps4__D_ cells (Fig 5B and below). In both backgrounds Sec2GEF-GFP-CUE expression leads to the formation of clusters of 80 nm vesicles that appear to correlate with the fluorescent puncta visible by light microscopy. The vps4__D _cells have in addition curved linear membrane structures that represent class E endosomes (see images at end of this file). The class E endosomes appear similar in cells expressing Sec2GEF-GFP-CUE, Sec2-GFP or Sec2. We did not observe any obvious spatial relationship between the class E structures and the vesicle clusters.

1. Discussion: "Furthermore, delivery of Mup1-GFP to the vacuole was slowed in Sec2GEF-GFP-CUE cells..." - The authors studied "the clearance of Mup1-GFP from the plasma membrane" and not vacuolar delivery. They did not show much vacuolar localization.

We now include quantitation of Mup1-GFP at both the plasma membrane and vacuole (Fig 6 and Fig S8). This shows a reduced rate of depletion from the plasma membrane and a delayed appearance in the vacuole.

Literature:<br /> Nagano, M., Toshima, J. Y., Siekhaus, D. E., & Toshima, J. (2019): Rab5-mediated endosome formation is regulated at the trans-Golgi network. Nature Communications Biology, 2 (1), 1-12.<br /> Nordmann, M., Cabrera, M., Perz, A., Bröcker, C., Ostrowicz, C., Engelbrecht-Vandré, S., & Ungermann, C. (2010): The Mon1-Ccz1 complex is the GEF of the late endosomal Rab7 homolog Ypt7. Current Biology, 20(18), 1654-1659.<br /> Paulsel, A. L., Merz, A. J., & Nickerson, D. P. (2013): Vps9 family protein Muk1 is the second Rab5 guanosine nucleotide exchange factor in budding yeast. Journal of Biological Chemistry, 288 (25), 18162-18171.<br /> Shideler, T., Nickerson, D. P., Merz, A. J., & Odorizzi, G. (2015): Ubiquitin binding by the CUE domain promotes endosomal localization of the Rab5 GEF Vps9. Molecular Biology of the Cell, 26 (7), 1345-1356.

Reviewer #1 (Significance):

• see above
• has some deficits in interpretation as the Rab relocalization was not complete and thus conclusions are limiting

Reviewer #2 (Evidence, reproducibility and clarity):

This paper tries to address a fundamental question in cell biology, namely, what machinery is sufficient to tell a vesicle know where to go and what to do when it gets there. Several groups have shown that localization of some Rab/Ypt GEFs to an orthogonal compartment can lead to redirecting a Rab/Ypt to that membrane, where they can bind their partners abnormally. This story tries to explore what happens next.

Here, Novick and colleagues took a part of the SEC2 GEF for secretory vesicle SEC4 Rab/Ypt and anchored it to endocytic structures to ask whether that was enough to relocalize those structures and drive inappropriate trafficking events. A challenge and advantage in the study is the fact that not all of the GEF relocalized-and that enables the cells to survive as SEC4p is needed for cell growth and membrane delivery--but this incomplete relocalization complicates phenotypic analysis--some SEC4 is on secretory vesicles and some is relocalized apparently to endocytic structures. Another challenge is that the two compartments both show "polarized" distributions so it is hard to know what compartment the reader is looking at, in a given figure. This makes the story very challenging to digest for a non-yeast expert trying to understand the conclusions.

The authors show that the CUE domain can serve to partially localize SEC2GEF-GFP-CUE and this function relies on its ability to interact with ubiquitin. The localization is distinct from that of full length Sec2, nonetheless "many structures bearing Sec2GEF-GFP-CUE localize close to the normal sites of cell surface growth despite their abnormal appearance". The authors conclude that SEC4p and its effectors were recruited to these puncta with variable efficiency and the puncta were static; normal secretion was not blocked. This is not really a surprise as some SEC4p is still directed to secretory granules and cells do not show a vesicle accumulation phenotype by EM. Missing seems to be a clear-cut visual assay for exocytosis of secretory granules or endocytic structures despite attempts to include live cell imaging.

We now show that the bright Sec2GEF-GFP-CUE_ puncta correspond to clusters of 80nm vesicles (Fig 5B). Our FRAP analysis demonstrates that Sec2GEF-GFP-CUE _is able to enter into pre-existing, bleached puncta (Fig 1E). One interpretation is that the vesicle cluster remains static, while individual vesicles enter and exit the cluster.

The authors showed that SEC2-GFP-CUE structures fail to acquire Sro7 and do not seem to be able to assemble a complex with the tSNARE SEC9. Is this because Sro7 is being retained on the remaining secretory vesicles that also have SEC4 and other effectors that may be recruited to those structures by coordinate recognition?

We demonstrate that at least half of the Sec2GEF-GFP-CUE puncta colocalize with Vps9 and this becomes even more evident in a vps4__D_ _mutant (Fig 2A). There is also substantial colocalization with the Rab5 homolog Ypt51, the endocytic marker Vps8 and PI(3)P (Fig 2 and Fig S3D). Nearly all of these puncta also colocalize with Sec4 and most of its downstream effectors. Thus, it seems that we have generated a hybrid compartment, as we intended. The surprise is how well the cells can cope with this situation. One possible explanation is offered in the Discussion: In yeast the TGN is thought to play the role of the early endosome and may be the site of Vps9 membrane recruitment. Thus Sec2GEF-GFP-CUE might be initially recruited to the TGN and the hybrid vesicles formed from this compartment might function to bring secretory cargo from the TGN to the cell surface just like normal secretory vesicles, with the caveat that the presence of endocytic machinery is somewhat inhibitory to Sro7 function, slowing fusion.

There seem to be no issues with data as presented; a diagram of the SEC2-GFP-CUE would help the reader as would use of terms "secretory vesicle" and "endocytic vesicle" and how they were always distinguished rather than "polarized structure" which cannot distinguish these compartments.

We have tried to be careful in our use of terms. We refer to the Sec2-GFP-CUE puncta using the unbiased terms “structures” or “puncta” until we show EM demonstrating that these puncta represent clusters of 80 nm vesicles.

CROSS-CONSULTATION COMMENTS<br /> The two assessments come to the same conclusion--I agree that better definition of the precise phenotypes could be valuable but the limitation of incomplete relocalization will be hard to overcome in the absence of enormous effort.

Reviewer #2 (Significance):

This story represents a valiant effort and presents clean data but the impact and significance of the findings are limited due to the difficult phenotypic starting points (SEC4 in two places), and lack powerful exo- or endocytosis assays and better compartment-specific markers.

The work will be of interest to yeast cell biologists studying the secretory and endocytic pathways. My expertise is mammalian cell biology of the secretory and endocytic pathways.

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Referee #2

Evidence, reproducibility and clarity

This paper tries to address a fundamental question in cell biology, namely, what machinery is sufficient to tell a vesicle know where to go and what to do when it gets there. Several groups have shown that localization of some Rab/Ypt GEFs to an orthogonal compartment can lead to redirecting a Rab/Ypt to that membrane, where they can bind their partners abnormally. This story tries to explore what happens next.

Here, Novick and colleagues took a part of the SEC2 GEF for secretory vesicle SEC4 Rab/Ypt and anchored it to endocytic structures to ask whether that was enough to relocalize those structures and drive inappropriate trafficking events. A challenge and advantage in the study is the fact that not all of the GEF relocalized-and that enables the cells to survive as SEC4p is needed for cell growth and membrane delivery--but this incomplete relocalization complicates phenotypic analysis--some SEC4 is on secretory vesicles and some is relocalized apparently to endocytic structures. Another challenge is that the two compartments both show "polarized" distributions so it is hard to know what compartment the reader is looking at, in a given figure. This makes the story very challenging to digest for a non-yeast expert trying to understand the conclusions.

The authors show that the CUE domain can serve to partially localize SEC2GEF-GFP-CUE and this function relies on its ability to interact with ubiquitin. The localization is distinct from that of full length Sec2, nonetheless "many structures bearing Sec2GEF-GFP-CUE localize close to the normal sites of cell surface growth despite their abnormal appearance". The authors conclude that SEC4p and its effectors were recruited to these puncta with variable efficiency and the puncta were static; normal secretion was not blocked. This is not really a surprise as some SEC4p is still directed to secretory granules and cells do not show a vesicle accumulation phenotype by EM. Missing seems to be a clear-cut visual assay for exocytosis of secretory granules or endocytic structures despite attempts to include live cell imaging.

The authors showed that SEC2-GFP-CUE structures fail to acquire Sro7 and do not seem to be able to assemble a complex with the tSNARE SEC9. Is this because Sro7 is being retained on the remaining secretory vesicles that also have SEC4 and other effectors that may be recruited to those structures by coordinate recognition?

There seem to be no issues with data as presented; a diagram of the SEC2-GFP-CUE would help the reader as would use of terms "secretory vesicle" and "endocytic vesicle" and how they were always distinguished rather than "polarized structure" which cannot distinguish these compartments.

Referees cross-commenting

The two assessments come to the same conclusion--I agree that better definition of the precise phenotypes could be valuable but the limitation of incomplete relocalization will be hard to overcome in the absence of enormous effort.

Significance

This story represents a valiant effort and presents clean data but the impact and significance of the findings are limited due to the difficult phenotypic starting points (SEC4 in two places), and lack powerful exo- or endocytosis assays and better compartment-specific markers.

The work will be of interest to yeast cell biologists studying the secretory and endocytic pathways. My expertise is mammalian cell biology of the secretory and endocytic pathways.

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Referee #1

Evidence, reproducibility and clarity

The manuscript from Li et al. describes the authors' attempt to redirect the exocytic Rab Sec4 to endocytic vesicles by fusing the GEF-domain of Sec2 to the CUE domain of the endosomal GEF Vps9, which binds to ubiquitin. The authors show that the localization of the Sec2GEF-GFP-CUE construct is slightly shifted from polarized towards non-polarized sites. Sec2GFP-CUE positive structures acquire Sec4 and Sec4 effectors like exocytic vesicles, but are less motile and show delayed plasma membrane fusion. Expression of Sec2GEF-GFP-CUE was enhanced if expressed in a subset of secretory and endocytic mutants and cause delayed Mup1 uptake from the plasma membrane. As Vps9, Sec2GEF-GFP-CUE accumulated on Class E compartments in vps4Δ strains.<br /> The authors ask here whether vesicular identity is largely predetermined by the correct localization of the specific GEFs of small GTPases and thus localization of the Rab. Although this an interesting hypothesis, the authors observed that endocytic traffic was not reversed by relocating Sec4 to these vesicles. This seems to be due to the strong affinity of the Sec2 GEF-domain for Sec4 but probably also due to the rather weak relocalization via the CUE domain. Thus, only a portion of Sec2 was displaced from its native site. Since the efficiency of this rewiring was not defined, it remains unclear whether the observed mild effects indeed speak against the assumed dominant role of the GEFs and small GTPases in shaping organelle identity or whether they are rather due to an inefficient relocalization.

Specific comments:

1. The authors state decidedly that the recruitment of Vps9 occurs ubiquitin-dependent via the CUE-domain. While the CUE-domain is the only known and a likely localization determinant of Vps9, it was not a strong localization determinant. Apart from being present in some puncta, Vps9 localized strongly to the cytosol (Paulsel et al. 2013, Nagano et al. 2019). Shideler et al. also showed that ubiquitin-binding is not required for Vps9 function in vivo, which indicates that other localizing mechanisms may play a role e. g. by positive feedback of GEF-domain-Rab5 interactions which might be initiated by the other Rab5-GEF Muk1 or as suggested by transport from the Golgi (Nagano et al. 2019). These observations indicate that the CUE-domain is a rather weak recruitment domain, which was not discussed in this manuscript. The localization of the Sec2GEF-GFP-control to the polarized sites in 30% of the cells furthermore suggests that the used Sec2GEF-GFP-CUE retains some native localization via the GEF-domain. Since the relocation efficiency of Sec2GEF-GFP-CUE was not defined, the obtained phenotypic effects allow for only vague conclusions. Although the mild endo- and exocytosis defects as well as the accumulation of Sec2GEF-GFP-CUE at Class E compartments indicate that the CUE-domain indeed conferred some relocation to endosomes, this was not shown for the sec2Δ strain e. g. by looking at colocalizations with endocytic versus exocytic markers and comparing their relative abundance at the Sec2GEF-GFP-CUE-positive structures. While some of the Sec2GEF-GFP-CUE-positive structures colocalized with Mup1 in the Mup1-uptake assay, it would be important to clarify how many endosomal properties are retained and how many exocytic properties are gained by these chimeric vesicles e. g. by looking for the presence of specific phosphoinositides, or Rab5 and Rab5 effectors. A competition between endosomal and the acquired exocytic factors could also be another possible explanation for the immobility of the Sec2GEF-GFP-CUE structures and less efficient recruitment of Sec4 effectors in addition to the proposed lack of PI4P.
2. While the colocalization of the Sec2GEF-GFP-CUE-signal with Sec4 indicates that this GEF-construct is generally active, it remains unclear whether the activity of the tagged constructs differ from that of the wild type Sec2 protein. This could be analyzed in vitro via a MANT-GDP GEF-activity assay (Nordmann et al., 2010). Again, it remains unclear how much of the Sec2GEF-Sec4 colocalization represents the retained native localization versus synthetic localization at chimeric endo-exocytic vesicles.
3. The authors mention that tagging with GFP increases the stability of the expressed constructs. However, it remains unclear whether this is also the case for the other tags (NeonGreen, mCherry) used in the other experiments. Are the constructs expressed at similar levels?
4. In Figure 5: The incomplete colocalization of Sec2GEF-GFP-CUE with Vps9 is explained by the short-timed accessibility of ubiquitin moieties. Apart from the likely retained native localization or weak CUE-domain-function, this observation could also be due to competition between Vps9 and Sec2GEF-GFP-CUE for the available ubiquitin target structures.

Minor remarks:

1. Fig. 3C do not contain the arrowheads as indicated in the legend, making it harder to interpret.
2. The image chosen for Sec2-GFP in Fig. 4B suggests less colocalization between Sec2-GFP and Sec8 than between Sec2GEF-GFP-CUE and Sec8. They rather look next to each other.
3. Figure 5: While resolution limits are possibly reached regarding endosomes, it might be interesting to check by thin section electron microscopy whether and how class E compartment formation is affected by Sec2GEF-GFP-CUE expression.
4. Discussion: "Furthermore, delivery of Mup1-GFP to the vacuole was slowed in Sec2GEF-GFP-CUE cells..." - The authors studied "the clearance of Mup1-GFP from the plasma membrane" and not vacuolar delivery. They did not show much vacuolar localization.

Literature:

Nagano, M., Toshima, J. Y., Siekhaus, D. E., & Toshima, J. (2019): Rab5-mediated endosome formation is regulated at the trans-Golgi network. Nature Communications Biology, 2 (1), 1-12.

Nordmann, M., Cabrera, M., Perz, A., Bröcker, C., Ostrowicz, C., Engelbrecht-Vandré, S., & Ungermann, C. (2010): The Mon1-Ccz1 complex is the GEF of the late endosomal Rab7 homolog Ypt7. Current Biology, 20(18), 1654-1659.

Paulsel, A. L., Merz, A. J., & Nickerson, D. P. (2013): Vps9 family protein Muk1 is the second Rab5 guanosine nucleotide exchange factor in budding yeast. Journal of Biological Chemistry, 288 (25), 18162-18171.

Shideler, T., Nickerson, D. P., Merz, A. J., & Odorizzi, G. (2015): Ubiquitin binding by the CUE domain promotes endosomal localization of the Rab5 GEF Vps9. Molecular Biology of the Cell, 26 (7), 1345-1356.

Significance

• see above
• has some deficits in interpretation as the Rab relocalization was not complete and thus conclusions are limiting

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

This manuscript by Gouignard et al., reports that a matrix metalloproteinase MMP28 regulates neural crest EMT and migration by transcriptional control rather than matrix remodeling. The manuscript is clearly written and provides sufficient evidence and control experiments to demonstrate that the MMP28 can translocate into nucleus of non-producing cells and that nuclear localization and catalytic activity are essential for the activity of MMP28 to regulate gene transcription. ChIP-PCR analysis also suggests that MMP28 can bind to the proximal promoters of Twist and others. However, since weak binding is also detected between MMP14 and the promoters, a more direct evidence that such binding can indeed promote Twist expression will be more appreciated.

Thank you for this comment. First, to represent the data from our ChIP assays we normalized all intensities to the GFP condition such that all levels are expressed fold change to GFP and we performed statistical comparisons. This shows that the enrichment of promoter regions by MMP28 and MMP14 are not equivalent.

Second, to substantiate our previous ChIP data, we performed a new set of ChIP experiments, by performing three independent chromatin immunoprecipitations (biological replicates), and used primers targeting three new domains in the proximal promoter of Twist and primers against two domains in the proximal promoter of E-cadherin and one domain 1kb away from transcription start of E-cadh. We found that pull down with MMP28 significantly enriches the three tested domains within the proximal promoter of Twist but not those of the E-cadherin promoter, compared to GFP pull down. These data were added to Figure 7.

However, we do not propose that MMP28 might act as a transcription factor and be able to promote Twist expression on its own. We apologize if some of the initial description of our data were too blunt and might have misled the reviewers. First, the protein sequence of MMP28, like those of all other MMPs, does not contain any typical DNA binding sites. In addition, ectopic overexpression of MMP28 is not sufficient to promote ectopic Twist expression (as shown in supplementary Figure 4) whereas, by contrast, Twist is able to promote ectopic expression of Cadherin-11 (see new Supplementary Figure 11). This indicates that MMP28 has an effect on Twist expression in the context of neural crest only and is not capable of activating Twist expression by itself.

Also, it should be added that enrichments of promoter domains by MMP28 pull-down are very modest in comparison to enrichments obtain with Twist pull-downs. Therefore, a more plausible role for MMP28 is to be part of a regulatory cascade with other factors involved in regulating the expression of the target genes important for EMT. Other MMPs such as MMP14 and MMP3 have been shown to interact with chromatin with some transcriptional downstream effects but multiple domains of these proteins seem to equally mediate such interactions. None of the data published in these studies rules out a relay via cofactors. We extensively modified the text describing our data and provided additional context.

Identifying the putative partners and their functional relationship with MMP28 is a project on its own and beyond the scope of this study.

While the nuclear translocation and transcription regulation activity of MMP28 is clearly the focus of the study, there are some minor issues that should be further clarified in the functional studies in the earlier part of the manuscript.

First, the effect of the splicing MO is somewhat unexpected. I would think that the splicing MO would lead to the retention of intron one and therefore premature termination or frameshift of the protein product, but RT-PCR or RT-qPCR suggest that there is no retention of intron 1, but a reduction in the full-length transcript, exon 1, or exon 7-8. Why is that?

Thank you for this comment. This is presumably due to nonsense mediated RNA decay. We have not explored the biochemistry of MMP28 RNA following injection with MOspl. Splicing MOs can have multiple effects. As explained on the GeneTools website splicing MOs disturb the normal processing of pre-mRNA and cells have various ways to deal with this and there are multiple possible outcomes. The PCR with E1-I1 suggests that intron 1 is not retained. Therefore, a putative concern would be that MOspl led to exon-skipping and to the generation of a truncated form of MMP28. However, we have checked that it is not the case. The fact that the PCR using E7-E8 primers indicates a reduction as well suggests an overall degradation of the mRNA for MMP28. Importantly, the effect of MOspl can be rescued using MMP28 mRNA indicating that the knockdown is specific.

Second, the effect of the splicing MO and ATG MO in NC explant spreading seems to be somewhat different, with ATG MO strongly repressed explant spreading, cell protrusion, and cell dispersion, while splicing MO does not affect cell dispersion, but affects the formation of cell protrusions. Does this reflects different severity of the phenotype or does the product of splicing MO display some activity?

Thank you for this comment. However, we think that there may be a confusion. Data on Fig2 (MOatg) and Fig3 (MOspl) both show a decrease of neural crest migration in vivo (Figure 2a-b) and of neural crest dispersion ex vivo (Fig2c, Fig3i-k). Along the course of the project we have never observed a difference in penetrance or intensity of the phenotypes between the two MOs.

Also, the switch between ATG MO and splicing MO is a bit confusing, maybe it is better to keep splicing MO only in the main text and move results involving ATG MO to supplementary studies.

The reason is purely historical. We had an effect with MOatg that can be rescued but there is no available anti-Xenopus MMP28 to assess its efficiency. So we turned to MOspl to have an internal control of efficiency by PCR. This provides an independent knockdown method reinforcing the findings. Both MOs have been controlled for specificity by rescue with MMP28 and display similar effect on NC migration/dispersion. We see no harm in keeping both in the main figures but if the reviewer feels strongly about this we could perform the suggested redistribution of data between main and supp figures.

Lastly, in Figure 3C and 3J, it says that the distance of migration or explant areas were normalized to CMO, while normalization against the contralateral uninjected side, or explant area at time 0 makes more sense.

Thank you for this comment as it will allow us to explain better these quantifications. Regarding in vivo measurements (Figure 3c), it is indeed the ratio between injected and non-injected sides that is performed in all conditions and then the ratios are normalized to CMO. We have now clarified this point on all instances throughout the figures.

Regarding ex vivo measurements (Figure 3j), NC explants are placed onto fibronectin and left to adhere for 1 hour before time-lapse imaging starts. NC cells extracted from MMP28 morphant embryos are not as efficient at adhering and spreading as control NC cells. Therefore, normalizing to t0 would erase that initial difference between control and MMP28 conditions. By normalizing to CMO at t_final we can visualize the initial defect of adhesion and spreading as well as the overall defects since CMO at t_final represents the 100% dispersion possible over the time course of the movie.

Referee Cross-commenting

I agree with comments from both Reviewers 2 and 3, especially that whether MMP28 regulates placode development (through Six1 expression) should be addressed.

Reviewer #1 (Significance):

This work provides novel insights of how a metalloprotease that is normally considered to function extracellularly can transfer into the nucleus of neighboring cells and regulate transcription. This would be of interest to researchers studying EMT, cell migration, and the functions of extracellular proteins in general. My expertise is in neural crest EMT and migration, and cytoskeletal regulation of cell behavioral changes. I do not have enough background on biochemical analysis.

Reviewer #2 (Evidence, reproducibility and clarity):

Summary:

In this study, Gouignard et al. beautifully use the Xenopus neural crest as a model system to examine the role of the matrix metalloproteinase MMP28 during EMT. The authors show that mmp28 is expressed by the placodes adjacent to the neural crest. Using in vivo and in vitro perturbation experiments, they show that the catalytic function of MMP28 is necessary for the expression of several neural crest markers, as well as neural crest migration and adhesion. Next, the authors use grafting, confocal imaging, and biochemistry to convincingly demonstrate that MMP28 is translocated into the nucleus of neural crest cells from the adjacent placodes. Finally, nuclear localization of MMP28-GFP is necessary to rescue twist and sox10 expression in MMP28 morphants, and ChIP-PCR experiments suggest direct interactions between MMPs and the proximal promoters of several neural crest genes. These results have significant implications on the field of EMT and highlight an underappreciated role for MMPs as direct regulators of gene expression.

Major comments:

Overall, the experiments presented in this study are thoroughly controlled and the results are clearly quantitated and rigorously analyzed. Most claims are well supported by multiple lines of experimental evidence; however, there are a few experiments or observations that this reviewer thinks should be reconsidered for more clarity and accuracy.

1. Supplementary Figure 1 shows the effect of MMP28-MOspl on additional ectodermal markers and shows that there is a significant loss of six1 expression from the placodal domain following MMP28 knockdown. The authors note this as a "slight reduction" on line 95, but since this shows a larger reduction in gene expression than some of the neural crest markers (snai2, sox8, foxd3), this reviewer thinks these results warrant a more significant discussion in this study.

Thank you for this comment. We apologize for the poor choice of word regarding the description of the effect on Six1 expression. We corrected the associated paragraph.

Although we do observe a reduction of Six1 expression upon MMP28 knockdown, this cannot explain the observed downregulation of some neural crest genes in our MMP28 experiments. There are noticeable differences between the effects of Six1 loss of function that have been reported in the literature and the MMP28 knockdown phenotypes we describe. As suggested by the reviewer, we added a paragraph in the discussion.

Does MMP28 localize to the nucleus of placodal cells as it does with neural crest? If so, is it through interaction with the six1 proximal promoter? If MMP28 does not localize to the nucleus, that would suggest MMP28 function with a different mechanism between epithelial cells distinct from role in EMT. These questions could be addressed by analysis of the placode cells in the images in Figure 5 and use of primers against the six1 proximal promoter on any remaining samples from the ChIP experiment.

Thank you for this comment. To address whether nuclear entry is specific to the neural crest-placodes interaction, we performed new grafts:

• 1/ we replaced neural crest cells from embryos expressing MMP28-GFP by placodal cells injected with Rhodamine-dextran. This generates grafted embryos with control placodes next to placodes overexpressing MMP28-GFP. There, we can analyze entry of MMP28-GFP in placodal cells that do not overexpress it. We detected MMP28 in the cytoplasm and in the nucleus of these placodal cells. However, the rate of nuclear entry was lower than in NC cells.

• 2/ To assess the importance of the cell type producing MMP28, we grafted NC cells injected with Rhodamine-dextran next to caudal ectoderm expressing MMP28-GFP. MMP28 was detected in cytoplasm and the nucleus of the NC cells but with a lower efficiency than when NC are grafted next to placodes expressing MMP28-GFP.

• 3/ We made animal caps sandwiches with animal caps injected with Rhodamine-dextran and animal caps expressing MMP28-GFP. In this case MMP28-GFP is detected in the cytoplasm but fails to reach the nucleus.

Collectively, these data indicate that placodes can import MMP28 produced by placodes and that NC can import MMP28 produced by other cells than placodes. However, in both cases the rate of nuclear entry was lower than in the NC-placode situation. Finally, the animal cap sandwiches indicate that entry into the cells does not predict entry into the nucleus. All these data were added to Supp Figure 7. Statistical comparisons of the proportion of cells with cytoplasmic and nuclear MMP28-GFP in all grafts were added to Figure 5.

The Six1 promoter analysis suggested is beyond the scope of this study as our focus is primarily on the role of MMP28 in neural crest development.

1. In Figure 2c, the authors rescue MMP28-MOatg with injection of MMP28wt mRNA. Does the MOatg bind to the exogenous mRNA? If so, this may just reflect titration of the MOatg. If this is the case, this experiment should be repeated with MOspl instead of MOatg.

Thank you for this comment. MOatg is designed upstream of the ATG and thus the binding site is not included in the expression construct. We added this important technical information in the methods. Of note, we already have the suggested equivalent of Fig2C with the MOspl on figure 3.

1. Is there a missing data point in Figure 2d corresponding to the upper bounds of the whisker in the 6 hour time point for the MMP28-MOatg dataset?

Thank you for pointing this out. The top data point was indeed missing from the graph, and we apologize for this oversight. We have now updated the figure with the correct graph.

1. The authors present ChIP-PCR results in Figure 7 as the major evidence to support the mechanism of nuclear MMP28 in regulating neural crest EMT through physical interaction with target gene promoters. However, the experimental design and presentation in Figure 7 are somewhat unconventional, and as such, difficult to interpret. First, instead of displaying the band brightness across the gel, the authors should normalize their bands to their negative GFP control, thus allowing for interpretation as a "fold enrichment over GFP control". It would be most clear to present these results in the form of a plot similar to Shimizu-Hirota et al., 2012, Figure 6D. Using qPCR instead of gel-based quantitation would further increase reproducibility by removing any bias in image analysis.

Thank you for this comment. For each band the value of the adjacent local background was subtracted. We have now normalized to GFP to provide graphs showing the fold change to GFP enrichment as requested.

However, we would like to point out that we do not propose that MMP28 might act as a transcription factor and be able to promote Twist expression on its own. First, the protein sequence of MMP28 does not contain any typical DNA binding sites, as is the case for any other MMPs. In addition, ectopic overexpression of MMP28 is not sufficient to promote ectopic Twist expression (see sup figure 4) contrary to Twist that can ectopically induce Cadherin-11 for instance (see sup figure 11). Further, enrichments of promoter domains by MMP28 pull downs are very modest in comparison of the enrichments promoted by Twist pull downs.

A more plausible role for MMP28 is that it is recruited via an interaction with other factors involved in regulating the expression of the target genes related to EMT. Identifying the partners and their functional relationship with MMP28 is a project on its own, and beyond the scope of this study.

Second, a proximal promoter sequence represents only ~250 bp upstream from the transcriptional start site. What is the rationale for testing multiple loci up to 3 kb upstream?

Thank you for pointing this out. The use of the term “proximal” was indeed misleading we have now corrected this part in the text. Regulatory sequences can be located anywhere so we initially had a broader approach to test for interactions. Following on this reviewer’s comment, we removed the data points corresponding to the very distal sites. In addition, we performed three new independent ChIP-PCR assays with primers in the proximal portion of Twist and E-cadherin promoters and found enrichment in ChIP with MMP28-GFP compared to GFP for Twist but not for E-cadherin (whose expression was not affected by MMP28 knockdown). These data were added to Figure 7.

It is surprising to see that most of these proteins do not show significant enrichment to a particular locus across this ~3 kb territory, while this reviewer would expect to see enrichment close to the TSS that quickly is lost as you move further upstream. Can you explain why MMP28, MMP14, and often Twist, show similar enrichment across this long genomic region?

Thank you for this comment. Our initial choice of representation did not allow to compare profiles properly. Fold-enrichment to GFP, as suggested by this reviewer, now shows that Twist, MMP28 and MMP14 do not display the same pattern of enrichment across the various loci and that MMP28 pull downs leads to significant enrichments of some of the domains tested in Cad11 and Twist promoters.

Third, the authors should include additional genomic loci to act as negative controls. For example, E-cadherin was unaffected by MMP28-MOspl, thus there may be no physical interaction between the E-cadherin locus and MMP28. It would be ideal to display results from at least one neural crest-related and one non-neural crest-related gene. Finally, this experiment requires statistical analyses to increase confidence in these interactions.

Thank you for this comment. We tested binding to E-cadherin promoter for GFP and MMP28-GFP and found no enrichment with MMP28. We also performed statistics as requested. These data were added to Figure 7.

Minor comments:

1. The authors should expand their abstract to more explicitly describe the experiments and results presented within this study.

Done

1. In the introduction, line 57 is unclear. "MMP28 is the latest member..." Is this chronologically? Evolutionarily? After this, the authors' statement that the roles of MMP28 are "poorly described" (lines 59-60) seems contradicting with their next sentences citing several studies that document the roles of MMP28 in diverse systems.

Thank you for this comment. The term “poorly described” was meant with respect to other MMPs with more extensive literature. We have now rephrased this part. Regarding the “latest member” we meant the last to be identified. We have now rephrased this part.

1. To increase clarity, the authors should define which cell types are labeled by in situ hybridization for sox10 and foxi4.1 in Figure 1e.

Thank you, we performed the requested clarifications and expanded the change to add the cell types labelled by the other genes used on the figure (see figure legend).

1. The PCR analysis for mmp28 splicing shown in Figure 1g is very clear and well demonstrates the efficacy of the MMP28-MOspl. However, the authors should note in the figure legend what the "ODC" row represents as this is unclear.

We added the definition of ODC in the figure legends and in the methods.

1. On line 118 the authors first reference "MOatg" but should explicitly define this reagent and its mechanism of action for clarity.

We performed the requested clarification.

Referee Cross-commenting

As with Reviewer #1, I was surprised that the RT-PCR analysis presented in support of the splicing MO lacked retention of intron one. I reasoned this might be due to reduced transcript abundance through a mechanism such as nonsense-mediated decay, but I agree that this data raises questions that the authors should address.

Thank you for this comment. Indeed, this is presumably due to nonsense mediated RNA decay. We have not explored the biochemistry of MMP28 RNA following injection with MOspl. Splicing MOs can have multiple effects. As explained on the GeneTools website splicing MOs disturb the normal processing of pre-mRNA and cells have various ways to deal with this and there are multiple possible outcomes. The PCR with E1-I1 suggests that intron 1 is not retained. Therefore, a putative concern would be that MOspl led to exon-skipping and to the generation of a truncated form of MMP28. However, we have checked that it is not the case. The fact that the PCR using E7-E8 primers indicates a reduction as well suggest an overall degradation of the mRNA for MMP28. Importantly, the effect of MOspl can be rescued using MMP28 mRNA indicating that the knockdown is specific.

I also agree with the other comments from Reviewers 1 and 3.

Reviewer #2 (Significance):

This study by Gouignard et al. provides compelling evidence for the role of MMP28 during neural crest EMT. As neural crest cells share similar EMT and migration mechanisms with cancer progression, they represent a powerful system in which to study these biological processes in vivo. Previous work on MMP function has focused primarily on extracellular matrix remodeling and the effect on cell migration, with less attention given to the role of MMPs during EMT. More recent reports in other systems have begun to elucidate a role for MMP translocation into the nucleus, indicating a surprising and novel mechanism for these proteins. This work would be of particular interest to audiences interested in cancer, cell, and developmental biology, as it highlights the importance of the non-canonical function of metalloproteinases during EMT and migration.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary

This study by Gouignard and colleagues explores the mechanisms involving the matrix-metalloprotease MMP28 in the epithelial-to-mesenchymal transition (EMT) of neural crest cells. Interestingly and provocatively, they focus not only on the extracellular functions of this protease but also on the roles of MMP28 in the nucleus. This in non-conventional sub-cellular localization is shared with other MMPs, but its significance remains poorly understood. Here, the authors show that the nuclear function of MMP28 impacts the expression of key EMT regulators in neural crest cells in vivo.

Using Xenopus laevis as a powerful animal model to explore the early development, the authors show that mmp28 expression is found in the ectodermal placodal tissue adjacent to the neural crest prior and after EMT.<br /> In the first part of the study, the authors show that MMP28 depletion affects a subset of neural crest marker gene expression (snai2, twi, sox10) but not others (sox9, snai1), suggesting a specific role on a subset of the genes important for neural crest EMT. The MMP28 depletion phenotype is restored by coinjecting MMP28 MO and MMP28 mRNA, provided that the catalytic activity of the encoded protein is maintained. Next, epistasis (rescue) experiments show that Twist1 can compensate MMP28 depletion.<br /> The second part of the study elegantly shows that MMP28 produced by host adjacent tissues can translocate into the nucleus of neural crest cells grafted from a donor embryo (devoid of MMP28-GFP expression). It also shows that MMP28 nuclear localization as well as its catalytic activity are both required for activating the neural crest gene twist1 and sox10; and that MMP28 is found bound on the chromatin of twist1, cad11 and sox10.<br /> Altogether, these experiments strongly support a model for the nuclear role of MMP28 in the activation (or maintenance) of key genes of the EMT program in vertebrate neural crest cells.

Major comments

The key conclusions are:

Conclusion 1: MMP28, expressed and secreted by placodes, is important for complete neural crest patterning prior to EMT, including activation of twist1 and EMT effector cadherin 11 genes. MMP28 is important for neural crest EMT and migration in vivo and in explant assay in vitro.

However, this conclusion omits potential indirect effect of interfering with placode formation itself, as indicated by the strong decrease in six1 expression in morphant embryos. The effect of MMP28MO on the expression of six1 is as strong as for neural crest markers snai2, twi, for example. Line 95, "slight reduction" should be modified.

Thank you or this comment. We have now modified the associated text.

What this may mean for placodal development itself, as well as for indirect effects on neural crest cells need to be discussed.

Following this comment, we added a paragraph in the discussion about Six1.

Conclusion 2: Gain of Twist 1 (but not Cadherin 11) rescues MMP28 morphant phenotype, allowing EMT to occur and restoring several parameters of cell migration in vivo and in explant assay

Conclusion 3: When secreted from adjacent cells, MMP28 is translocated into the nucleus of neural crest cells and displays a nuclear function important for the activation of twist1 expression.

Both conclusions 2 and 3 are supported by multiple elegant and convincing experimental data. These conclusions do not depend on mmp28 exclusive expression by the placodal ectoderm, and would still be important if there was a minor expression in the neural crest cells themselves (and thus an autocrine effect).

Additional experiments to strengthen the conclusions<br /> Related to Conclusion 1:

• line 102-106: In the rescue experiment, is six1 expression rescued too?

Thank you for this comment. As detailed in the newly added discussion paragraph about the effects of Six1 loss of function that have been described in the literature, it is very unlikely that our NC phenotypes stem from the observed reduction of Six1 expression.

Nonetheless, following this comment we checked for Six1 expression in the placodal domain following MMP28 knockdown and rescue condition. In the rescue condition, only 25% of the embryos had recovered Six1 expression in placodes while 75% of the embryos recovered Sox10 expression in neural crest cells. These data further confirm that rescue of placodal genes is not a pre-requisite for the rescue of neural crest genes and were added in Supp Figure 5.

Although MMP28 is likely to have a role in placodes as well, the expansion of Sox2 and Pax3 expression domain and the loss of Eya1 expression typically associated with Six1 knockdown did not occur in MMP28 knockdown. Our story being focused on neural crest cells, we did not investigate further how the MMP28-dependent effect on Six1 might impair placode development.

• Figure 2g: qPCR analysis suggests that mmp28 is expressed in the neural crest explants themselves, levels being lowered by the MO injection. The levels of this potential expression in the neural crest itself should be compared to the levels in the placodal ectoderm. How do the authors exclude an effect of the MO within the neural crest tissue, independently of roles from the placodal tissue?

Thank you for this comment. There is a very small subpopulation of NC cells called the medial crest that expresses MMP28. They are along a thin line along the edge of the neural folds. We previously described this in Gouignard et al Phil Trans Royal Soc B 2020. It is useful for us as an internal control for MO efficiency but the expression in placodes is much stronger and involves many more cells. However, this expression called our attention at the onset of the project and we performed some experiments to assess whether some of the observed effects were due to a NC-autonomous effect, as suggested by this reviewer. To test for this we performed targeted injected of the MO such that the medial crest would receive the MO but not the placodes. Targeting the medial crest with MMP28-MO had no effect on Sox10 expression. These data were added to new supp Figure 1.

The cost and time for these additional experiments is limited (about 3 weeks), and uses reagents already available to the authors.

Data and Methods are described with details including all necessary information to replicate the study. Replication is carefully done and statistical analysis seems convincing.

Minor comments

Experimental suggestions to further strengthen the conclusions.<br /> Related to Conclusion 1: - Figure 1e, frontal histological sections would help distinguishing between placodal tissue and neural crest mesenchyme.

Thank you for this comment. We previously published a detailed expression pattern with such sections (Gouignard et al Phil Trans Royal Soc B, 2020). We rephrased the text to better refer to this previous publication.

Related to Conclusion 2: - Figure 3: in explants co-injected with twist1 mRNA, is cad11 expression restored? Could this indicate if cad11 is (or is not) part of the program controlled by Twist1 (as suggested by the last main figure)?

Thank you for this comment. We checked for Cadherin-11 expression in control MO, MMP28-MOspl and MOspl+Twist mRNA and Twist is indeed capable of inducing Cadherin-11 and even leads to ectopic activation of Cad11 on the injected side. These data were added to new Supp Figure 11.

Related to Conclusion 3: is MMP28 translocation seen in any cell context? Could the authors repeat experiments in Figure 6a with animal cap ectoderm? And with sandwich animal cap ectoderm, one expressing MMP28-GFP versions (wt, deltaSPNLS) and the other Rhodamine Dextran only? This would allow to generalize the mechanism or on the contrary to show a neural crest specificity.

Thank you for this comment. Following this suggestion and comments from the other reviewers, we performed new grafting experiments.

• 1/ we replaced neural crest cells from embryos expressing MMP28-GFP by placodal cells injected with Rhodamine-dextran. This generates grafted embryos with control placodes next to placodes overexpressing MMP28-GFP. There, we can analyze entry of MMP28-GFP in placodal cells that do not overexpress it. We detected MMP28 in the cytoplasm and in the nucleus of these placodal cells. However, the rate of nuclear entry was lower than in NC cells.
• 2/ To assess the importance of the cell type producing MMP28 we grafted NC cells injected with Rhodamine-dextran next to caudal ectoderm expressing MMP28-GFP. MMP28 was detected in cytoplasm and the nucleus of the NC cells but with a lower efficiency than when NC are grafted next to placodes expressing MMP28-GFP.
• 3/ We made animal caps sandwiches with animal caps injected with Rhodamine-dextran and animal caps expressing MMP28-GFP. In this case MMP28-GFP is detected in the cytoplasm but fails to reach the nucleus. These data indicate that placodes can import MMP28 produced by placodes and that NC can import MMP28 produced by other cells than placodes. However, in both cases the rate of nuclear entry was lower than in the NC-placode situation. Finally the animal cap sandwiches indicate that entry into the cells does not predict entry into the nucleus. All these data were added to new Supp Figure 7 and quantifications of import of MMP28-GFP in the cytoplasm and the nucleus all conditions added to Figure 5.

In supplementary figure 4a, the grey (RDx) is not visible in the zoom in images.

As the grey channel interferes with visualizing the green channel, we only show the grey channel on the first low magnification image so that the position of grafted cells can be seen. We found it better to omit it from the zoomed in images to avoid masking the GFP signal.

In figure 7a,b MMP14 is green, GFP is grey (mentioned wrongly in line 276)

Thank you for pointing this out. We have extensively modified Figure 7 and such issues are now resolved.

Bibliographical references are accurate. Clarity of the text and figures is excellent, except maybe Figure 7, where a qPCR analysis would be easier to visualize, especially with low-level or fuzzy bands on the gel.

Thank you. We have now modified Figure 7, including normalization to GFP to show fold-change enrichment and have added new data from three independent ChIP assays for proximal Twist and E-cadherin promoters that we hope further substantiate our initial observations.

Reviewer #3 (Significance):

Place of the work in the field's context:

In cancer, the MMP proteins are widely described in multiple tumor contexts and promote cell invasion. In development, several studies have focused on their functions in the extracellular space. The nuclear localization of MMP family proteins has been described previously but remained poorly understood so far. This work is thus a pioneer study aiming to understand MMP28 nuclear function.

Advance:

This study makes a significant advance in the field, by unraveling the importance of the MMP28 activity in the cell nucleus for the expression of key EMT regulators. Moreover, the study suggests that extracellular MMP28 secreted by adjacent cells or tissues can be internalized and transported to cell nucleus into cells located several cell diameters away. This study thus supports a novel facet of MMP proteins activity, complementary to their previously described role on the extracellular matrix, and further favoring cell invasion, in development and potentially in cancer too.

The target audience goes without doubt beyond developmental biologists (the primary interest) and also includes cell and cancer biologists, and any biologist interested by MMPs or cell invasion mechanisms in vivo.

My field of expertise is developmental biology focused on neural and neural crest early development, mainly using animal models in vivo and some cell culture experiments. I also focus on some aspects of cancer cell migration.

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Referee #3

Evidence, reproducibility and clarity

Summary

This study by Gouignard and colleagues explores the mechanisms involving the matrix-metalloprotease MMP28 in the epithelial-to-mesenchymal transition (EMT) of neural crest cells. Interestingly and provocatively, they focus not only on the extracellular functions of this protease but also on the roles of MMP28 in the nucleus. This in non-conventional sub-cellular localization is shared with other MMPs, but its significance remains poorly understood. Here, the authors show that the nuclear function of MMP28 impacts the expression of key EMT regulators in neural crest cells in vivo.

Using Xenopus laevis as a powerful animal model to explore the early development, the authors show that mmp28 expression is found in the ectodermal placodal tissue adjacent to the neural crest prior and after EMT.<br /> In the first part of the study, the authors show that MMP28 depletion affects a subset of neural crest marker gene expression (snai2, twi, sox10) but not others (sox9, snai1), suggesting a specific role on a subset of the genes important for neural crest EMT. The MMP28 depletion phenotype is restored by coinjecting MMP28 MO and MMP28 mRNA, provided that the catalytic activity of the encoded protein is maintained. Next, epistasis (rescue) experiments show that Twist1 can compensate MMP28 depletion.<br /> The second part of the study elegantly shows that MMP28 produced by host adjacent tissues can translocate into the nucleus of neural crest cells grafted from a donor embryo (devoid of MMP28-GFP expression). It also shows that MMP28 nuclear localization as well as its catalytic activity are both required for activating the neural crest gene twist1 and sox10; and that MMP28 is found bound on the chromatin of twist1, cad11 and sox10.<br /> Altogether, these experiments strongly support a model for the nuclear role of MMP28 in the activation (or maintenance) of key genes of the EMT program in vertebrate neural crest cells.

Major comments

The key conclusions are:

Conclusion 1: MMP28, expressed and secreted by placodes, is important for complete neural crest patterning prior to EMT, including activation of twist1 and EMT effector cadherin 11 genes. MMP28 is important for neural crest EMT and migration in vivo and in explant assay in vitro.

However, this conclusion omits potential indirect effect of interfering with placode formation itself, as indicated by the strong decrease in six1 expression in morphant embryos. The effect of MMP28MO on the expression of six1 is as strong as for neural crest markers snai2, twi, for example. Line 95, "slight reduction" should be modified. What this may mean for placodal development itself, as well as for indirect effects on neural crest cells need to be discussed.

Conclusion 2: Gain of Twist 1 (but not Cadherin 11) rescues MMP28 morphant phenotype, allowing EMT to occur and restoring several parameters of cell migration in vivo and in explant assay

Conclusion 3: When secreted from adjacent cells, MMP28 is translocated into the nucleus of neural crest cells and displays a nuclear function important for the activation of twist1 expression.

Both conclusions 2 and 3 are supported by multiple elegant and convincing experimental data. These conclusions do not depend on mmp28 exclusive expression by the placodal ectoderm, and would still be important if there was a minor expression in the neural crest cells themselves (and thus an autocrine effect).

Additional experiments to strengthen the conclusions<br /> Related to Conclusion 1:

• line 102-106: In the rescue experiment, is six1 expression rescued too?
• Figure 2g: qPCR analysis suggests that mmp28 is expressed in the neural crest explants themselves, levels being lowered by the MO injection. The levels of this potential expression in the neural crest itself should be compared to the levels in the placodal ectoderm. How do the authors exclude an effect of the MO within the neural crest tissue, independently of roles from the placodal tissue?

The cost and time for these additional experiments is limited (about 3 weeks), and uses reagents already available to the authors.

Data and Methods are described with details including all necessary information to replicate the study. Replication is carefully done and statistical analysis seems convincing.

Minor comments

Experimental suggestions to further strengthen the conclusions.<br /> Related to Conclusion 1: - Figure 1e, frontal histological sections would help distinguishing between placodal tissue and neural crest mesenchyme.<br /> Related to Conclusion 2: - Figure 3: in explants co-injected with twist1 mRNA, is cad11 expression restored? Could this indicate if cad11 is (or is not) part of the program controlled by Twist1 (as suggested by the last main figure)?<br /> Related to Conclusion 3: is MMP28 translocation seen in any cell context? Could the authors repeat experiments in Figure 6a with animal cap ectoderm? And with sandwich animal cap ectoderm, one expressing MMP28-GFP versions (wt, deltaSPNLS) and the other Rhodamine Dextran only? This would allow to generalize the mechanism or on the contrary to show a neural crest specificity.

In supplementary figure 4a, the grey (RDx) is not visible in the zoom in images.<br /> In figure 7a,b MMP14 is green, GFP is grey (mentioned wrongly in line 276)<br /> Bibliographical references are accurate. Clarity of the text and figures is excellent, except maybe Figure 7, where a qPCR analysis would be easier to visualize, especially with low-level or fuzzy bands on the gel.

Significance

Place of the work in the field's context:

In cancer, the MMP proteins are widely described in multiple tumor contexts and promote cell invasion. In development, several studies have focused on their functions in the extracellular space. The nuclear localization of MMP family proteins has been described previously but remained poorly understood so far. This work is thus a pioneer study aiming to understand MMP28 nuclear function.

Advance:

This study makes a significant advance in the field, by unraveling the importance of the MMP28 activity in the cell nucleus for the expression of key EMT regulators. Moreover, the study suggests that extracellular MMP28 secreted by adjacent cells or tissues can be internalized and transported to cell nucleus into cells located several cell diameters away. This study thus supports a novel facet of MMP proteins activity, complementary to their previously described role on the extracellular matrix, and further favoring cell invasion, in development and potentially in cancer too.

The target audience goes without doubt beyond developmental biologists (the primary interest) and also includes cell and cancer biologists, and any biologist interested by MMPs or cell invasion mechanisms in vivo.

My field of expertise is developmental biology focused on neural and neural crest early development, mainly using animal models in vivo and some cell culture experiments. I also focus on some aspects of cancer cell migration.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, Gouignard et al. beautifully use the Xenopus neural crest as a model system to examine the role of the matrix metalloproteinase MMP28 during EMT. The authors show that mmp28 is expressed by the placodes adjacent to the neural crest. Using in vivo and in vitro perturbation experiments, they show that the catalytic function of MMP28 is necessary for the expression of several neural crest markers, as well as neural crest migration and adhesion. Next, the authors use grafting, confocal imaging, and biochemistry to convincingly demonstrate that MMP28 is translocated into the nucleus of neural crest cells from the adjacent placodes. Finally, nuclear localization of MMP28-GFP is necessary to rescue twist and sox10 expression in MMP28 morphants, and ChIP-PCR experiments suggest direct interactions between MMPs and the proximal promoters of several neural crest genes. These results have significant implications on the field of EMT and highlight an underappreciated role for MMPs as direct regulators of gene expression.

Major comments:

Overall, the experiments presented in this study are thoroughly controlled and the results are clearly quantitated and rigorously analyzed. Most claims are well supported by multiple lines of experimental evidence; however, there are a few experiments or observations that this reviewer thinks should be reconsidered for more clarity and accuracy.

1. Supplementary Figure 1 shows the effect of MMP28-MOspl on additional ectodermal markers and shows that there is a significant loss of six1 expression from the placodal domain following MMP28 knockdown. The authors note this as a "slight reduction" on line 95, but since this shows a larger reduction in gene expression than some of the neural crest markers (snai2, sox8, foxd3), this reviewer thinks these results warrant a more significant discussion in this study. Does MMP28 localize to the nucleus of placodal cells as it does with neural crest? If so, is it through interaction with the six1 proximal promoter? If MMP28 does not localize to the nucleus, that would suggest MMP28 function with a different mechanism between epithelial cells distinct from role in EMT. These questions could be addressed by analysis of the placode cells in the images in Figure 5 and use of primers against the six1 proximal promoter on any remaining samples from the ChIP experiment.
2. In Figure 2c, the authors rescue MMP28-MOatg with injection of MMP28wt mRNA. Does the MOatg bind to the exogenous mRNA? If so, this may just reflect titration of the MOatg. If this is the case, this experiment should be repeated with MOspl instead of MOatg.
3. Is there a missing data point in Figure 2d corresponding to the upper bounds of the whisker in the 6 hour time point for the MMP28-MOatg dataset?
4. The authors present ChIP-PCR results in Figure 7 as the major evidence to support the mechanism of nuclear MMP28 in regulating neural crest EMT through physical interaction with target gene promoters. However, the experimental design and presentation in Figure 7 are somewhat unconventional, and as such, difficult to interpret. First, instead of displaying the band brightness across the gel, the authors should normalize their bands to their negative GFP control, thus allowing for interpretation as a "fold enrichment over GFP control". It would be most clear to present these results in the form of a plot similar to Shimizu-Hirota et al., 2012, Figure 6D. Using qPCR instead of gel-based quantitation would further increase reproducibility by removing any bias in image analysis. Second, a proximal promoter sequence represents only ~250 bp upstream from the transcriptional start site. What is the rationale for testing multiple loci up to 3 kb upstream? It is surprising to see that most of these proteins do not show significant enrichment to a particular locus across this ~3 kb territory, while this reviewer would expect to see enrichment close to the TSS that quickly is lost as you move further upstream. Can you explain why MMP28, MMP14, and often Twist, show similar enrichment across this long genomic region? Third, the authors should include additional genomic loci to act as negative controls. For example, E-cadherin was unaffected by MMP28-MOspl, thus there may be no physical interaction between the E-cadherin locus and MMP28. It would be ideal to display results from at least one neural crest-related and one non-neural crest-related gene. Finally, this experiment requires statistical analyses to increase confidence in these interactions.

Minor comments:

1. The authors should expand their abstract to more explicitly describe the experiments and results presented within this study.
2. In the introduction, line 57 is unclear. "MMP28 is the latest member..." Is this chronologically? Evolutionarily? After this, the authors' statement that the roles of MMP28 are "poorly described" (lines 59-60) seems contradicting with their next sentences citing several studies that document the roles of MMP28 in diverse systems.
3. To increase clarity, the authors should define which cell types are labeled by in situ hybridization for sox10 and foxi4.1 in Figure 1e.
4. The PCR analysis for mmp28 splicing shown in Figure 1g is very clear and well demonstrates the efficacy of the MMP28-MOspl. However, the authors should note in the figure legend what the "ODC" row represents as this is unclear.
5. On line 118 the authors first reference "MOatg" but should explicitly define this reagent and its mechanism of action for clarity.

Referee Cross-commenting

As with Reviewer #1, I was surprised that the RT-PCR analysis presented in support of the splicing MO lacked retention of intron one. I reasoned this might be due to reduced transcript abundance through a mechanism such as nonsense-mediated decay, but I agree that this data raises questions that the authors should address.

I also agree with the other comments from Reviewers 1 and 3.

Significance

This study by Gouignard et al. provides compelling evidence for the role of MMP28 during neural crest EMT. As neural crest cells share similar EMT and migration mechanisms with cancer progression, they represent a powerful system in which to study these biological processes in vivo. Previous work on MMP function has focused primarily on extracellular matrix remodeling and the effect on cell migration, with less attention given to the role of MMPs during EMT. More recent reports in other systems have begun to elucidate a role for MMP translocation into the nucleus, indicating a surprising and novel mechanism for these proteins. This work would be of particular interest to audiences interested in cancer, cell, and developmental biology, as it highlights the importance of the non-canonical function of metalloproteinases during EMT and migration.

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Referee #1

Evidence, reproducibility and clarity

This manuscript by Gouignard et al., reports that a matrix metalloproteinase MMP28 regulates neural crest EMT and migration by transcriptional control rather than matrix remodeling. The manuscript is clearly written and provides sufficient evidence and control experiments to demonstrate that the MMP28 can translocate into nucleus of non-producing cells and that nuclear localization and catalytic activity are essential for the activity of MMP28 to regulate gene transcription. ChIP-PCR analysis also suggests that MMP28 can bind to the proximal promotors of Twist and others. However, since weak binding is also detected between MMP14 and the promoters, a more direct evidence that such binding can indeed promote Twist expression will be more appreciated.

While the nuclear translocation and transcription regulation activity of MMP28 is clearly the focus of the study, there are some minor issues that should be further clarified in the functional studies in the earlier part of the manuscript.

First, the effect of the splicing MO is somewhat unexpected. I would think that the splicing MO would lead to the retention of intron one and therefore premature termination or frameshift of the protein product, but RT-PCR or RT-qPCR suggest that there is no retention of intron 1, but a reduction in the full-length transcript, exon 1, or exon 7-8. Why is that?

Second, the effect of the splicing MO and ATG MO in NC explant spreading seems to be somewhat different, with ATG MO strongly repressed explant spreading, cell protrusion, and cell dispersion, while splicing MO does not affect cell dispersion, but affects the formation of cell protrusions. Does this reflects different severity of the phenotype or does the product of splicing MO display some activity? Also, the switch between ATG MO and splicing MO is a bit confusing, maybe it is better to keep splicing MO only in the main text and move results involving ATG MO to supplementary studies.

Lastly, in Figure 3C and 3J, it says that the distance of migration or explant areas were normalized to CMO, while normalization against the contralateral uninjected side, or explant area at time 0 makes more sense.

Referee Cross-commenting

I agree with comments from both Reviewers 2 and 3, especially that whether MMP28 regulates placode development (through Six1 expression) should be addressed.

Significance

This work provides novel insights of how a metalloprotease that is normally considered to function extracellularly can transfer into the nucleus of neighboring cells and regulate transcription. This would be of interest to researchers studying EMT, cell migration, and the functions of extracellular proteins in general. My expertise is in neural crest EMT and migration, and cytoskeletal regulation of cell behavioral changes. I do not have enough background on biochemical analysis.

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Reply to the reviewers

1. General Statements [optional]

*All three referee reports are very supportive. The referees acknowledge the insight obtained for NF2 tumor suppressor function, and they state unanimously that the appeal to the broader audience stems from the systematic deep mutational scanning approach employed. *

Indeed, the goal of the study was to utilize conformation dependent NF2 protein interaction partners as a read out in deep mutational scanning interaction perturbation, which lead to the identification of an novel region, the F3 part of the FERM domain, important for NF2 conformation. The referees recognized the advance of the study and provided constructive feedback with excellent opportunities to improve the manuscript.

*The points raised by the referees relate to the deep scanning analyses which needs additional explanations. Referee 1 has several comments with respect to experimental details, which we will address through text revisions and addition of data. Referee 2 suggests to include the Y2H in full (as supplemental part) and asks for more methodological discussion. We plan to include the data and will provide a new advantage / disadvantage discussion section for the deep scanning results. This is in line with Referee 3 who similarly says that “the deep mutational scanning interaction perturbation assay … message is somewhat lost in the main text”. *

2. Description of the planned revisions

Referee 1:

In his/her first point the referee asks about justification of the use of the kinase in the Y2H experiments. Here we will report in more detail which kinases were used, in fact it was a discovery that ABL2 in contrast to all others tested did promote the NF2-PIK3R3 interaction. However, in the manuscript we provide evidence that the kinase dependency does not necessarily relate to NF2 phosphorylation. Rather we find mutations that relieved the PIK3R3-NF2 interaction from the kinase dependency. We show that the kinase promotes the PIK3R3 dimerization. We will make this point more clear in text revisions.

We want to address the minor points 1-3 and 6-8 through revisions in the text, as we feel confident that the points can be addressed through better explanations and more detail.

*Point 4: *

We have examined expression of the YFP construct and will include the data in the revision.

*Point 5: *

We will reexamine the fluorescence images and provide better resolution pictures. Depending on the data we have, this may include new data were we record the localization of the NF2 variants again at higher resolution.

Referee 2:

Point 1: The bait construct which is missing from the panel was tested, but is autoactive and therefore the result can not be included in the figure. This will be clearly stated in the manuscript.

*Point 2: The methodological part of the paper is important, however we failed to provide a discussion on the deep scanning result and agree that a critical discussion of advantages and disadvantages is warranted. *

Minor points 1,2,4,5,6,7,9,10,12,13,14,15 can be addressed in full through text revisions.

Point 3: Data will be added to supplemental Figure S1, however as we mentioned in the main text, the Iso1N and Iso7N, when used as prey do not result any interactions.

Point 8: Taking the suggestion of the referee on board, we will provide a new Supplemental figure showing all variants that did not change the interaction patterns.

*Point 11: We will fix the inconsistencies in Figure 5. We will include Q147 in the overall structure, S265 is a surface residue providing little structural information. *

Referee 3:

We thank referees 3 for their time and effort providing an assessment as experts on the molecular and clinical aspects of NF2.

In response to the comments, we will strengthen the deep mutational scanning message through a new critical discussion part and fix the mistakes pointed at in the text.

*We agree with the referees that “The use of isoform 7 as a construct is helpful to locate protein binding regions, but its physiological relevance is unclear.” This is exactly the point, to use a non-tumor suppressive isoform as a construct contrasting the binding behavior of the canonical isoform 1. We tried to summarize the knowledge about the non-canonical isoforms in the introduction (page2 bottom to page 3 top paragraph) as well as in Supplemental Figure 1. Unfortunately literature information is sparse. *

Finally, we will check carefully (again) whether we used isoform 1 numbering throughout the manuscript.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors developed a deep mutational scanning interaction perturbation technique, based on reverse yeast two-hybrid analysis, to identify important regions influencing conformation dependent protein function in NF2.

They test the tumor suppressive NF2 isoform 1 and a shorter non-tumor suppressive isoform 7 (lacking exons 2 and 3 and containing exon 16 instead of 17) and find three interacting proteins, KDM1A, EMILIN1 and PIK3R3 (KDM1A and EMILIN1 have been identified previously). They map binding regions of these proteins using fragments of NF2 isoforms 1 and 7 and by large-scale interaction perturbation mutation scanning.

Major comments:

The main scientific advancement in the study is the development of the deep mutational scanning interaction perturbation assay, but this message is somewhat lost in the main text of the results.

The relevance of the binding protein that did not bind isoform 1 is unclear (PIK3R3) and the relevance of characterising the binding domains for three proteins with an unknown function is not made clear. Were these the only binding partners identified in the yeast screen? The use of isoform 7 as a construct is helpful to locate protein binding regions, but its physiological relevance is unclear. Does it have known expression or a known function in human cells?

Minor comments:

Nomenclature should be updated in line with the new guidelines (i.e. NF2 vs neurofibromin)

The two major isoforms are 1 and 2, differentiated by their C-terminal region (exon 17 or Exon 16). It would be helpful to describe protein binding regions using the amino acid numbering of the full-length transcripts throughout the manuscript, rather than using isoform 7 numbering in some sections.

"Closeness", should perhaps be changed to closed-ness

The significance of the RT4-D6P2T and HEI-193 cell lines should be explained/indicated in the text.

PPI should be expanded at first use.

Results are included in the context of previous studies, but it needs to be made clearer in some places which results were found in previous studies and which were identified in the current study.

Specific recommendations

1. 'NF2 (Neurofibromine 2, merlin)' -delewte 'neurofibromine' this has been deleted by HGNC
2. 'Genetic mutations or deletion of NF2 cause neurofibromatosis type 2,' -Replace neurofibromatosis type 2 with NF2 related-schwannomatosis and cite Legius et al Genet Med 2022

Referees cross-commenting

I cannot see any changes to this manuscript. In particular the terms 'neurofibromine' and neurofibromatosis should be deleted

Significance

The authors developed a deep mutational scanning interaction perturbation technique, based on reverse yeast two-hybrid analysis, to identify important regions influencing conformation dependent protein function in NF2.

They test the tumor suppressive NF2 isoform 1 and a shorter non-tumor suppressive isoform 7 (lacking exons 2 and 3 and containing exon 16 instead of 17) and find three interacting proteins, KDM1A, EMILIN1 and PIK3R3 (KDM1A and EMILIN1 have been identified previously). They map binding regions of these proteins using fragments of NF2 isoforms 1 and 7 and by large-scale interaction perturbation mutation scanning.

The main scientific advancement in the study is the development of the deep mutational scanning interaction perturbation assay, but this message is somewhat lost in the main text of the results.

Dr Smith and Professor Evans are experts on the molecular and clinical aspects of NF2

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Referee #2

Evidence, reproducibility and clarity

Summary

In this manuscript the authors describe the use of a reverse Y2H-based, systematic mutational analysis method to study effects on conformation-dependent interactions of the NF2 tumor suppressor protein. Using this approach, they identified regions important for NF2 protein interaction and homomer formation and correlated some of these with cellular proliferation and matched patterns of known disease mutations. Overall, this work provides useful insight into NF2 tumor suppressor function (by identifying amino acids critical for NF2 conformational regulation) while demonstrating the power of their mutational scanning approach.

Major Comments

1. Why does Figure 1b not include interaction results for the NF2-Iso1N fragment as bait? Did the authors test this?
2. The authors state that the majority of retested interactions behaved like WT (i.e., could not be confirmed; page 7 last paragraph) and claim this may be due to a difference in sensitivity between the deep scanning screen and pair wise spot testing. This seems like a very vague justification for the differences between the two assays; also, it's not immediately clear to me that the high-throughput scanning assay would necessarily be more sensitive than the lower-throughput pairwise comparison assay. The authors should provide a bit more discussion on this and address the possibility of false positives in their deep mutational scanning assay.

Minor Comments

1. Page 4, Line 3 from the bottom - should ready 'three isoform-specific protein interaction partners' not 'partner'.
2. In Figure 1b, the interaction of NF2-Iso7-ex17 with PIK3R3 in the absence of ABL3 suggests that the observed kinase-dependence interaction of the NF2-Iso7 form may actually not be solely due to PIK3R3 homodimerization driven by phosphorylation. The authors should make note of this possibility in the text.
3. On page 5 the authors mention that Iso1N and Iso7N, when used as preys, did not interact with full-length NF2. I don't see this experiment in the figures, however.
4. On Page 6 (first paragraph) the authors state that the PIK3R3 interaction was 'promoted through pY-dependent PIK3R3 homodimerization'. While this is a likely and reasonable conclusion, they haven't explicitly shown this, so they should be careful about making such a strong statement. I'd recommend saying 'likely promoted' or something similar instead.
5. In Figure S2, the Iso7 / EMILIN1 interaction does not appear to be giving the expected result in the rY2H (i.e., there is strong growth under both Y2H and r2H conditions). The authors should comment on/acknowledge this.
6. For the deep mutagenesis screen, why wasn't an ABL2 condition used for NF2-Iso1C (see Fig. S2b)?
7. For KDM1A and EMILIN1 the authors ran mutagenesis screens with both active and kinase dead ABL2, yet results were pooled. Were any differences observed in the effects of mutations on interaction between the two kinase conditions?
8. Why aren't the yeast plates shown for most of the unconfirmed interactions? These could still be included in the Supplementary Material.
9. On page 7, under Assessing Single Site Mutations, the authors refer to the Q147E mutation and reference Figure 3. However, Figure 3 shows only a Q147A mutation. Q147A is also referred to elsewhere. Which is the correct mutation?
10. Figure S3b shows the 20 mutations presented in Figure 3. The DMS row indicates that some of these did not produce perturbations in the DMS experiments. Perhaps I'm misunderstanding here, but weren't the 20 mutations shown (and 60 total mutations) selected based on activity in the DMS assay? Or did some of the ones selected correspond to mutations which not produce an effect? Please clarify in the text.
11. Why was the S265 mutation not considered in the structural analysis (other than being shown in Figure 4a, it isn't discussed). Also, Q147 (in the F2 region) is discussed and shown in Figure 4b, but not shown in the larger overall structure in Figure 4a.
12. The cell proliferation results are very difficult to meaningfully interpret. While it is clear that certain mutations do affect proliferation, consistency between different types of experiments and cell lines appears to be low.
13. Perhaps a bit more discussion of the possible consequences of using yeast to study human NF2 interactions and how these might affect results would be useful (i.e., due to differences in membrane composition, cellular environment, post-translational modifications etc. between yeast and mammalian cells).
14. Page 13, line 10 says 'your hypothesis'. Believe should read 'the hypothesis'.
15. Page 13, line 15 refers to '15' NF2 variants showing altered PPI patterns; however, 16 were described in the manuscript.

Significance

This work provides insight into how NF2 conformational changes relate to tumor suppressor function, which is particularly valuable since this area is still not well understood and published results have sometimes appeared contradictory. In addition to the insights into NF2 biology provided, the manuscript also demonstrates the value of the deep scanning mutagenesis approach. Overall, the presented research is very solid and, assuming the comments presented above (most of which are minor) are addressed I have no trouble recommending it for publication.

I believe that the NF2 biology section will be of interest to a more specialized audience, while the general demonstration of the utility of the deep scanning mutagenesis will have broader appeal.

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Referee #1

Evidence, reproducibility and clarity

The manuscript "Missense variant interaction scanning reveals a critical role of the FERM-F3 domain for tumor suppressor protein NF2 conformation and function" examines the effect of a reasonably exhaustive set of point mutations on the NF2 protein on protein-protein interactions and intra-protein interactions for two isoforms of NF2 (1 and 7), finding an interesting pattern of mutations in the region not associated with bindings nevertheless impact binding, and that this binding is sometimes dependent on the presence of kinase ABL2. Authors justify this by arguing conformation shifts in the protein, potentially regulated by phosphorylation, and with distinct conformations between isoforms 1 and 7 creating different interaction patterns, must explain the differences in binding properties. The paper specifically examines mutations to phosphomimetic (i.e., charged, so as to mimic phosphorylation) amino acid residues, with relevance for the probable biological regulation of this binding. Authors note that previous work has found inconsistent protein binding properties for phosphomimetic or phosphor-inhibiting substitutions on S518, in different conditions, which would be explained by other regulation of these conformational changes, a reasonable argument. Structural modeling of the mutants and their potential effects on a "closed" NF2 structure are intriguing and well-appreciated to support the paper's conclusions, and the paper is overall well-reasoned and convincing, and it should be published.

Concerns:

The kinase ABL2 is used to perturb NF2 phosphorylation, and this is not adequately justified. Kinases such as PAK2 (PMID: 11782491, PMID: 11719502) and PKA (PMID: 14981079) target NF2. In the methods referred to (Grossmann et al), nine tyrosine kinases were used for their screen, and while ABL2 was used in this paper and generated numerous interactions, it is not clear that ABL2 is the appropriate kinase to use here. The exhaustive use of many kinases would obviously be impractical and unreasonable for this study, but the choice of this kinase should be clearly explained.

Minor issues:

1. In the intro, authors write "While the other ERM protein family members do not have activities directly linked to cancer, NF2 tumor suppressor activity was initially characterized in flies and mice". While "directly" makes the statement technically true, it could be argued that ERM protein involvement is as legitimate as the tumor suppression activity of NF2 (PMID: 11092524, PMID: 24421310), and therefore the suggested contrast is slightly misleading. This has no relevance to the broader paper or its findings.
2. Figure 2b: Authors state mutational coverage is fairly even across the protein, however there appears to be a notable spike around a.a. 180? This does not match any of the site mutations later found to be particularly relevant for interactions, which cluster around 250 and 450, and is therefore not a significant issue.
3. In the methods, cell concentration is at one point said to be 'concentrated to an OD600 of 40-80'. I have never seen cell concentration expressed this way. Authors no doubt grew cells to an OD between 1 and 2 and concentrated ~40-fold as is standard, and wish perhaps to avoid estimating concentrations as cell numbers, which would only be approximate and cell size-dependent? However, OD is only linear between 1 and 2 for cell concentrations. An OD above 4 simply cannot be observed, as all light would be blocked. Methodology here is sound, this is merely an unusual way of expressing things.
4. Page 10: The authors point out that they cannot see any difference in the expression levels of the NF2 mutants. However there is no quantification of the immunofluorescence signal supporting this information. Maybe a western blot could suffice this argument.
5. It is very difficult to see the localization of NF2 mutants with the immunofluorescence images as they are very small. May be try with a 63X objective or focusing on just one or two cells or adding insets with higher magnification would allow the reader to view the details of Nf2 localization.
6. 5th line from the bottom on page 8: allowed to model -> allowed us to model
7. Line 8 from the top on page 12: inY2H -> in Y2H
8. Line 10 from the top on page 13: your hypothesis -> our hypothesis

Significance

Dear Editor,

The manuscript "Missense variant interaction scanning reveals a critical role of the FERM-F3 domain for tumor suppressor protein NF2 conformation and function" examines the effect of a reasonably exhaustive set of point mutations on the NF2 protein on protein-protein interactions and intra-protein interactions for two isoforms of NF2 (1 and 7), finding an interesting pattern of mutations in the region not associated with bindings nevertheless impact binding, and that this binding is sometimes dependent on the presence of kinase ABL2. Authors justify this by arguing conformation shifts in the protein, potentially regulated by phosphorylation, and with distinct conformations between isoforms 1 and 7 creating different interaction patterns, must explain the differences in binding properties. The paper specifically examines mutations to phosphomimetic (i.e., charged, so as to mimic phosphorylation) amino acid residues, with relevance for the probable biological regulation of this binding. Authors note that previous work has found inconsistent protein binding properties for phosphomimetic or phosphor-inhibiting substitutions on S518, in different conditions, which would be explained by other regulation of these conformational changes, a reasonable argument. Structural modeling of the mutants and their potential effects on a "closed" NF2 structure are intriguing and well-appreciated to support the paper's conclusions, and the paper is overall well-reasoned and convincing, and it should be published.

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Reply to the reviewers

Response to reviewers' comments

We thank the reviewers for their constructive evaluation of our manuscript. In the following point-by-point response, we explain how we will implement the suggested modifications.

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

Summary:

The formation of meiotic double-stranded DNA breaks is the starting point of meiotic recombination. DNA breaks are made by the topoisomerase-like SPO11, which interacts with a number of regulatory factors including REC114, MEI4 and IHO1. Despite the key role this process has in the continuation, and genetic variation, or eukaryotic life, there is very little known about how this process is regulated. Laroussi et al make use of biochemical, biophysical and structural biological approaches to extensively characterise the REC114-MEI4-IHO1 complex.

This is an outstanding biochemical paper. The experiments are well planned and beautifully executed. The protein purifications used are very clean, and the figures well presented. Importantly Laroussi et. al describe, and carefully characterise through point mutational analysis, the direct physical interaction between IHO1 and REC114-MEI4. This is an interaction that has, at least in yeast, previously been suggested to be driven by liquid-liquid separation. The careful and convincing work presented here represents an important paradigm-shift for the field.

I am fully supportive of publication of this excellent and important study.

We thank the reviewer for his/her positive comments, appreciation of the importance of our study and suggested modifications.

Major comments:

Point 1:

My only major concern is regarding Figure 4, and specifically the AF2 model of the coiled-coil tetramer of IHO1. Given the ease with which MSAs of coiled-coils can become "contaminated" with non-orthologous sequences, I would urge some caution with this model. This is especially since the yeast ortholog of IHO1, Mer2, has been previously reported to be an anti-parallel tetramer (albeit, not very well supported by the data). The authors have several choices here. 1) They could simply reduce the visibility of the IHO1 tetramer model, and indicate caution in the parallel tetramer model. 2) They could consider using a structure prediction algorithm that doesn't use an MSA (e.g. ESMFold). 3) They could try to obtain experimental evidence for a parallel coiled-coil tetramer, e.g. through EM, SAXS or FRET approaches. I would like to make it crystal clear, however, that I would be *very* supportive of approach 1) or 2). An experimental approach is *not* necessary.

Assuming the authors don't take a wet-lab approach, this shouldn't take more than a couple of weeks.

This is a very good suggestion. We are aware of the previously reported anti-parallel architecture of the yeast IHO1 ortholog Mer2 (Claeys Bouuaert et al., Nature 2021). It should be noted, that in the recent preprint, posted by the Claeys Bouuaert lab (BioRxiv, https://doi.org/10.1101/2022.12.16.520760), a high confidence model of yeast Mer2 (and for human) parallel tetrameric coliled-coil is presented, apparently consistent with their previous XL-MS results (Claeys Bouuaert et al., Nature 2021).

To clarify this issue we will follow the suggestions of Reviewer 1 and 2.

1. As suggested also by Reviewer 2, we will produce a tethered dimer of IHO1125-260, connected by a short linker and determine its MW by SEC-MALLS (and SAXS).
2. In the meantime we followed the suggestion of Reviewer 1 and modelled the IHO1130-281 by the ESMfold, which is another recent powerful AI-based program that does not use multiple sequence alignments. Remarkably, the predicted structure is very similar to the one predicted by AlphaFold, also predicting the parallel arrangement of IHO1. This model will be included as a supplementary figure.
3. We will also point out in the text that these models, despite being very convincing, remain models.

   Minor comments:

Point 2:

The observation that REC114 and MEI4 can also form a 4:2 complex is very interesting and potentially important. Did the authors also try to model this higher order complex in AF2?

Yes, we did this with the hope that we could identify residues whose mutation could limit the fast exchange between the 2:1 and 4:2 states. Unfortunately, no convincing additional contacts are modelled by AlphaFold. This PAE plot will be included as a supplementary figure.

Point 3:

Similarly to above, what does the prediction of the full-length REC114:MEI4 2:1 complex look like? Presumably the predicted interaction regions align well with experimental data, but it would be interesting to see (and easy to run).

The AlphaFold modelling of the FL REC114:MEI4 (2:1) complex will be included as supplementary figure. It is consistent with the model comprising only the interacting regions. No additional convincing contacts are predicted.

Point 4:

Did the authors carry out SEC-MALS experiments on any IHO1 fragment lacking the coiled-coil domain? It was previously reported for Mer2 that the C-terminal region can form dimers, for example (OPTIONAL).

We can easily do that. We have the N- and C- terminal regions lacking the coiled-coil expressed as MBP fusions and they will be analysed by SEC-MALLS.

Point 5:

Given that full-length REC114 is used for the IHO1 interaction studies, do the authors have any data as to the stoichiometry of the REC114FL-MEI41-127 complex? (OPTIONAL)

We have repeatedly analysed the REC114-MEI4-IHO1 complex sample by SEC-MALLS and native mass spectrometry, but in both cases the sample is too complex to be interpreted. This is like due to the fast exchange between REC114-MEI4 2:1 and 4:2 complexes and low binding affinity of IHO1 for REC114.

Point 6:

Did the authors try AF2 modelling of the REC114-IHO1 interaction using orthologs from other species?

Yes, but not extensively. We will repeat this modelling again.

**Referees cross commenting**

I will add cross-comments to the comments of Reviewer #2

Firstly, the comments made by Reviewer #2 are technically correct. Firstly, reviewer #2 points out that the oligomerization states that the authors report could, in part, be artifactual the based on the his-tag purification method. This is indeed correct. However, given that none of the oligomerization states reported are per se unusual, given what is already known (including pre-prints from the Keeney and Claeys Bouuaert laboratories), I think the authors could forego this step.

Secondly, the use of an experimental structural method, such as SAXS, would certainly add value to the paper. Also Reviewer #2 is correct in pointing out the availability of the ESRF beamlines to the authors. However, while SAXS is a useful method, I personally consider the use of mutants to validate the interactions, an even stronger piece of evidence that the AlphaFold2 interactions are correct. I must disagree somewhat with Reviewer #2 with their argument that SAXS would validate the fold. Certainly if one of the AF2 predicted structures is radically wrong, then SAXS would produce scattering data, and a subsequent distance distribution plot that is incompatible with the AF2 model. However, a partly correct AF2 model, of roughly the right shape, might still fit into a SAXS envelope.

Reviewer #2 shares my concern on the parallel coiled-coil of IHO1, and their suggested solution is very elegant.

In my view, due to the time constraints imposed by the partially competing work from the Keeney and Claeys Bouuaert laboratories (recently on biorxiv). I would support the authors if they chose the quickest route to publication.

Reviewer #1 (Significance (Required)):

General assessment: The strengths of the paper are as follows:

1) Quality of experiments - The proteins used have been properly purified (SEC) and properly handled. The experiments are carefully carried out and controlled.

2) Detail - The authors carry out the considerable effort of characterising protein interactions. through separation-of-function mutants. This adds to the quality of the paper, and renders the AF2 models as convincing as experimentally determined structures

3) Conceptual advances - The most important conceptual advance is the direct binding of the N-term of IHO1 to REC114. That this is the same region as used by both TOPOVIBL and ANKRD31 points to a complex regulation.

4) Integrity - the authors have taken great care not to "oversell" the results. The data are presented, and analysed, without hyperbole.

Limitations - The only limitation of the paper is the lack of in vivo experiments to test their findings. However given the time and effort required, and the pressing need to publish this exciting study, this is not a problem.

Advance: The paper provides advances from a number of directions, both conceptual and mechanistic. Mechanistically the description of the REC114-MEI14 complex is important, and in particular the observation that it can also form a higher order 4:2 structure. Likewise, while IHO1 was inferred to be a tetramer (based on work on Mer2) this was never proven formally. Most importantly, is the physical linkage between IHO1 and REC114, and that this is an interaction that is incompatible with TOPOVIBL and ANKRD31.

Audience:

Given the central role of meiotic recombination in eukaryotic life, any studies that shed additional light on the regulation of meiosis are suitable for a broad audience. However, this subject paper will be more specifically of interest to the meiosis community. The elegant methodology will also be of interest to structural biologists and protein biochemists.

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

This manuscript addresses the structure of the REC114-MEI4-IHO1 complex, which controls the essential process of programmed DSB induction by SPO11/TOPOVIBL in meiosis.

The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.

We thank the reviewer for his/her positive comments on our study and the suggestions below.

I have two general suggestions:

Point 1:

Analyses have been performed on fusion proteins (His, His-MBP etc). we have previously observed that bulky tags such as MBP can interfere with oligomeric state through steric hindrance, and that His-tags can mediated formation of larger oligomers, seemingly through coordination of metals leached from IMAC purification. This latter point has also been observed by others

https://www.sciencedirect.com/science/article/pii/S1047847722000946.

Where possible, I would repeat SEC-MALS experiments using untagged proteins, or at least following incubation with EDTA to mitigate the potential for His-mediated oligomerization.

We agree with this reviewer’s comment that expression tags can have unexpected impact of the protein behaviour.

1. For REC114-MEI4 complex the stoichiometry is assessed by several techniques. Figure 1f,g shows analytical ultracentrifugation, which was performed on the minimal REC114226-254-MEI41-43 complex that contains no fusion tag showing that this stoichiometry is independent of fusion tags. We will nevertheless repeat the SEC-MALLS on REC114-MEI41-127 after removing the His-tag of MEI4 as suggested.
2. For the REC114 dimer, we cannot remove the His-MBP tag since this short fragment of REC114226-254 is no stable without MBP. The dimerization of Rec114 was already reported in (Claeys Bouuaert et al., Nature 2021). The dimerization is sensitive to specific point mutations within REC114. We will however, repeat the SEC-MALLS experiment following incubation with EDTA to mitigate the potential for His-mediated oligomerization.
3. The presented SEC-MALLS on IHO1 fragments (Figure 4b) was done on proteins without fusion tags. Reviewer 1 and 2 also agreed that additional repeats of the experiments without fusion tags are not necessary.

The authors have relied upon mutagenesis to validate Alphafold2 models. Their results are convincing but only confirm that contacts involved in structures rather than the specific fold per se. Their finding would be greatly strengthen by collecting SEC-SAXS data and fitting models directly to the scattering data. This is extremely sensitive, so a close fit provides the best possible evidence of accuracy of the model. SAXS is affected by unstructured regions and tags, so would have to be performed using structural cores of untagged proteins rather than full-length constructs. Given the local availability of world-class SAXS beamlines at the ESRF, which is next door to the leading author's institute, it seems that the collection of SAXS data would be practical for them.

The usage of SAXS is discussed in the specific points below. We will attempt to do SEC-SAXS on the REC114-MEI4 complex. Due to instability of REC114226-254 without MBP, SAXS cannot be done. We will also do SAXS on the IHO1 tetramer.

My specific comments are below:

Point 2:

Figure 1d

The SEC-MALS shows multiple species, with 2:1 and 4:2 representing a minority of total species present. What are the larger oligomers? Could these be an artefactual consequence of the His-tags (as described above)?

This SEC-MALLS will be repeated without the His-tag on MEI4.

Point 3:

Figure 1f,g

The AUC changes over concentration and pH are intriguing - have they tried MALS in these conditions? This would be much more informative as it would reveal the range of species present. Low concentrations could be analysed by peak position even if scattering is insufficient to provide interpretable MW fits. I would advise doing this without his tag or adding EDTA (as described above).

We will perform this experiment as suggested.

Point 4:

Figure 2

I would like to see the models validated by SAXS using minimum core untagged constructs. This could be sued to test the validity of the 2:1 model directly, and to model the 4:2 complex by multiphase analysis and/or docking together of 2:1 complexes.

The hydrophobic LALALAII region of MEI4 is interesting and the mutagenesis data do agree with the model. However, it is important to point out that any decent model would place this hydrophobic helix in the core of the complex, and so would be disrupted by mutagenesis. Hence, the mutagenesis results confirm that the hydrophobic helix is critical for the interaction, but does not confirm that the specific alphafold model is more valid than any other model in which the helix is similarly in a core position.

We will attempt to perform the SEC-SAXS measurements. The challenge here will be obtaining a sample that is monodisperse in solution being required for SAXS. We showed the fast exchange between the 2:1 and 4:2 oligomeric state. The AUC data indicates that the sample has a predominantly 2:1 stoichiometry at 0.2 mg/ml, pH 4.5 and 500mM NaCl. Given the small size of the complex, the signal at 0.2 mg/ml is likely to be noisy.

Point 5:

Figure 3

This would also benefit from SAXS validation of the structural core. The mutagenesis here provides convincing evidence in favour of the structure as specific hydrophobics ether disrupt or have no effect, exactly as predicted. Hence, their data strongly support the dimer model. As this provides the framework for the 2:1 complex, these data make me far more confident of the previous 2:1 model in figure 2. I am wondering whether it would be better to present these data first such that the reader can see the 2:1 model being built upon these strong foundations?

We agree with this suggestion and will present the REC114 dimerization data before the REC114-MEI4 complex. However, REC114226-254 is not stable without the MBP tag so is not suitable for SAXS analysis.

Point 6:

Figure 4

The MALS data convincingly show formation of a tetramer. How do we know that it is parallel? The truncation supports this but coiled-coils do sometimes form alternative structures when truncated (e.g. anti-parallel can become parallel when sequence is removed), and alphafold seems to have a tendency of predicting parallel coiled-coils even when the true structure of anti-parallel (informal observation by us and others). A simple test would be to make a tethered dimer of 110-240, with a short flexible linker between two copies of the same sequence - if parallel it should form a tetramer of double the length, if anti-parallel it should form a dimer of the same length - determinable by MALS (and SAXS).

To address this point we will perform this experiment as suggested by Reviewer 2. We will produce a tethered dimer of IHO1 110-240, connected by a short linker and determine its MW by MALS (and possibly SAXS). We also performed ESMfold modelling (Reviewer 1, Point 1), resulting in the same model. As the IHO1 tetramer is likely suitable for SAXS analysis, we will also perform SAXS on it.

Point 7:

Figures 5/6

The interaction is clear albeit low affinity (but within the biologically interesting range). It would be nice to obtain MALS (using superose 6) data showing the stoichiometry of the complex - are the data too noisy to be interpretable owing to dissociation? The alpahfold model and mutagenesis data strongly support the conclusion that the IHO1 N-term binds to the PH domain, as presented.

We have repeatedly analysed the REC114-MEI4-IHO1 complex sample by SEC-MALLS (on Superose 6) and native mass spectrometry, but in both cases the sample is too complex to be interpreted. This is likely due to the fast exchange between REC114-MEI4 2:1 and 4:2 complexes and low binding affinity of IHO1 for REC114.

**Referees cross commenting**

Just to clarify a couple of points regarding consultation comments from reviewer 1:

The suggestion regarding tags was mostly directed to the cases in which MALS data are noisy, with multiple oligomeric species (such as figure 1d). In these cases, i wondered whether the large MW species may be artefactual and could be resolved by removal of the tags. In cases where oligomers agree with those reported by other labs, I agree that there's no need to explore these further.

In terms of SAXS, I agree that fitting models into envelopes will not distinguish between similar folds. However, fitting models directly to raw scattering data is extremely sensitive and I have never seen good fits with low chi2 values for incorrect models (even when very similar in overall shape to the correct structure).

Reviewer #2 (Significance (Required)):

The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.

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

Laroussi et al used Alphafold models to predict the assembly of REC114-MEI4-IHO1 complex, and verified the structure using different biochemical experiments. Both Alphafold predictions and experiment data are convincing for the overall protein complex assembly. Importantly, they identified a motif on IHO1 that share the same binding site on REC114 with TOPOVIBL and ANKRD31, suggesting that REC114 acts as a regulatory base coordinating different binding partners during meiosis progression. Overall, I believe this is a nice biochemistry paper, but lacks insights into the biology (I believe those in vivo data is beyond the scope of this paper), at least more discussions are needed in terms of these findings.

We thank the reviewer for the supportive comments on our manuscript and its evaluation. We agree with the reviewer, that including in vivo data, that might provide further biological insights, would be useful. However, there is currently no good cellular model for meiotic recombination in mouse and thus our structure-based mutations will need to be tested in transgenic mice. Such data will take a long time to obtain and would delay the publication these in-vitro results that already provide novel insight into the REC114-MEI4-IHO1 complex architecture. We will, nevertheless, as suggested, strengthen the discussion of the biological implications of our findings.

Some minor points:

Point 1:

Any data showing MEI4 forms a dimer on its own?

As mentioned in the manuscript, full-length MEI4 is difficult to produce in bacteria or insect cells. Thus, we worked with the N-terminal fragment which in absence of REC114 is nor very stable. We will perform SEC-MALLS to assess its oligomeric state. Alphafold suggests dimeric arrangement of MEI4, but only with low confidence.

Point 2:

In Fig2 and Sup Fig4, HisMBP-MEI4, you see more MBP than the fusion protein, especially more obvious in the mutants. What's your explanation?

The N-terminus of MEI4 is well produced when co-expressed with REC114. For the pull-down experiments in Figure 2 we expressed it as His-MBP fusion in absence of REC114. In this situation, there is a degradation between MBP and MEI4. We find this very often for proteins that not very stable, which is the case of MEI4 without REC114. This is the best way we could produce at least some MEI4 in absence of REC114. The MBP protein could probably be removed by other chromatography techniques, but we think that for the purpose of the pull-down its presence is not interfering with the REC114-MEI4 binding.

Point 3:

TOPOVIBL and ANKRD31, I am curious if you have looked at the conserved residues on these motifs.

We show a strong conservation of the IHO1 among vertebrates (Fig. 6c). We will further analyse the sequence conservation in more distant species.

Point 4:

Reference needed when stating that IHO1 was not interacting with REC114 in previous biochemical assay in the discussion part.

This will be corrected

Point 5:

Also, have you run AlphaFold that gives multiple models? Sometimes, with short motifs, 1 or 2 models of several models give good confidence for the interaction.

Using in-house Alphafold installation producing 25 models did not reveal better models.

Reviewer #3 (Significance (Required)):

While most of the interactions between REC114 and MEI4 or IHO1 were established with Y2H or other biochemical assays before. This paper used the AlphaFold, and finally verified the findings with biochemical experiments, which helps to establish the exact motifs/residues involved in the interaction. For example, the MEI4-REC114 interfaces are novel, more interestingly, the IHO1 shares the same interface with ANKRD31 and TOPOVIBL. Thus, this finding of REC114-MEI4-IHO1 complex assembly would be interesting to people with different working areas. I would like to see more studies on the coordination IHO1 with ANKRD31 or TOPOVIBL in the future.

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

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Referee #3

Evidence, reproducibility and clarity

Laroussi et al used Alphafold models to predict the assembly of REC114-MEI4-IHO1 complex, and verified the structure using different biochemical experiments. Both Alphafold predictions and experiment data are convincing for the overall protein complex assembly. Importantly, they identified a motif on IHO1 that share the same binding site on REC114 with TOPOVIBL and ANKRD31, suggesting that REC114 acts as a regulatory base coordinating different binding partners during meiosis progression. Overall, I believe this is a nice biochemistry paper, but lacks insights into the biology (I believe those in vivo data is beyond the scope of this paper), at least more discussions are needed in terms of these findings.

Some minor points:

Any data showing MEI4 forms a dimer on its own? In Fig2 and Sup Fig4, HisMBP-MEI4, you see more MBP than the fusion protein, especially more obvious in the mutants. What's your explanation? Nice finding on the IHO1 N terminus, which shares the same binding sites on REC114 with TOPOVIBL and ANKRD31, I am curious if you have looked at the conserved residues on these motifs. Reference needed when stating that IHO1 was not interacting with REC114 in previous biochemical assay in the discussion part. Also, have you run AlphaFold that gives multiple models? Sometimes, with short motifs, 1 or 2 models of several models give good confidence for the interaction.

Significance

While most of the interactions between REC114 and MEI4 or IHO1 were established with Y2H or other biochemical assays before. This paper used the AlphaFold, and finally verified the findings with biochemical experiments, which helps to establish the exact motifs/residues involved in the interaction. For example, the MEI4-REC114 interfaces are novel, more interestingly, the IHO1 shares the same interface with ANKRD31 and TOPOVIBL. Thus, this finding of REC114-MEI4-IHO1 complex assembly would be interesting to people with different working areas. I would like to see more studies on the coordination IHO1 with ANKRD31 or TOPOVIBL in the future.

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 structure of the REC114-MEI4-IHO1 complex, which controls the essential process of programmed DSB induction by SPO11/TOPOVIBL in meiosis.

The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.

I have two general suggestions:

1. Analyses have been performed on fusion proteins (His, His-MBP etc). we have previously observed that bulky tags such as MBP can interfere with oligomeric state through steric hindrance, and that His-tags can mediated formation of larger oligomers, seemingly through coordination of metals leached from IMAC purification. This latter point has also been observed by others https://www.sciencedirect.com/science/article/pii/S1047847722000946. Where possible, I would repeat SEC-MALS experiments using untagged proteins, or at least following incubation with EDTA to mitigate the potential for His-mediated oligomerisation.
2. The authors have relied upon mutagenesis to validate Alphafold2 models. Their results are convincing but only confirm that contacts involved in structures rather than the specific fold per se. Their finding would be greatly strengthen by collecting SEC-SAXS data and fitting models directly to the scattering data. This is extremely sensitive, so a close fit provides the best possible evidence of accuracy of the model. SAXS is affected by unstructured regions and tags, so would have to be performed using structural cores of untagged proteins rather than full-length constructs. Given the local availability of world-class SAXS beamlines at the ESRF, which is next door to the leading author's institute, it seems that the collection of SAXS data would be practical for them.

My specific comments are below:

Figure 1d The SEC-MALS shows multiple species, with 2:1 and 4:2 representing a minority of total species present. What are the larger oligomers? Could these be an artefactual consequence of the His-tags (as described above)?

Figure 1f,g The AUC changes over concentration and pH are intriguing - have they tried MALS in these conditions? This would be much more informative as it would reveal the range of species present. Low concentrations could be analysed by peak position even if scattering is insufficient to provide interpretable MW fits. I would advise doing this without his tag or adding EDTA (as described above).

Figure 2 I would like to see the models validated by SAXS using minimum core untagged constructs. This could be sued to test the validity of the 2:1 model directly, and to model the 4:2 complex by multiphase analysis and/or docking together of 2:1 complexes. The hydrophobic LALALAII region of MEI4 is interesting and the mutagenesis data do agree with the model. However, it is important to point out that any decent model would place this hydrophobic helix in the core of the complex, and so would be disrupted by mutagenesis. Hence, the mutagenesis results confirm that the hydrophobic helix is critical for the interaction, but does not confirm that the specific alphafold model is more valid than any other model in which the helix is similarly in a core position.

Figure 3 This would also benefit from SAXS validation of the structural core. The mutagenesis here provides convincing evidence in favour of the structure as specific hydrophobics ether disrupt or have no effect, exactly as predicted. Hence, their data strongly support the dimer model. As this provides the framework for the 2:1 complex, these data make me far more confident of the previous 2:1 model in figure 2. I am wondering whether it would be better to present these data first such that the reader can see the 2:1 model being built upon these strong foundations?

Figure 4 The MALS data convincingly show formation of a tetramer. How do we know that it is parallel? The truncation supports this but coiled-coils do sometimes form alternative structures when truncated (e.g. anti-parallel can become parallel when sequence is removed), and alphafold seems to have a tendency of predicting parallel coiled-coils even when the true structure of anti-parallel (informal observation by us and others). A simple test would be to make a tethered dimer of 110-240, with a short flexible linker between two copies of the same sequence - if parallel it should form a tetramer of double the length, if anti-parallel it should form a dimer of the same length - determinable by MALS (and SAXS).

Figures 5/6 The interaction is clear albeit low affinity (but within the biologically interesting range). It would be nice to obtain MALS (using superose 6) data showing the stoichiometry of the complex - are the data too noisy to be interpretable owing to dissociation? The alpahfold model and mutagenesis data strongly support the conclusion that the IHO1 N-term binds to the PH domain, as presented.

Referees cross commenting

Just to clarify a couple of points regarding consultation comments from reviewer 1:

The suggestion regarding tags was mostly directed to the cases in which MALS data are noisy, with multiple oligomeric species (such as figure 1d). In these cases, i wondered whether the large MW species may be artefactual and could be resolved by removal of the tags. In cases where oligomers agree with those reported by other labs, I agree that there's no need to explore these further.

In terms of SAXS, I agree that fitting models into envelopes will not distinguish between similar folds. However, fitting models directly to raw scattering data is extremely sensitive and I have never seen good fits with low chi2 values for incorrect models (even when very similar in overall shape to the correct structure).

Significance

The manuscript carefully combines biochemistry, biophysics and modelling in an integrative manner to report the architecture of the full REC114-MEI4-IHO1 complex that is not itself amenable to direct structure elucidation such as by X-ray crystallography. These are important results that will be of interest to the recombination and meiosis fields. The data are generally convincing and interpretations appear correct, so the manuscript is certainly suitable for publication. I have included some suggestions below that I believe would strengthen the manuscript and enhance our confidence in the findings. Whilst the manuscript is publishable in its current format, I believe the suggestions given below would make it into a much stronger paper.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The formation of meiotic double-stranded DNA breaks is the starting point of meiotic recombination. DNA breaks are made by the topoisomerase-like SPO11, which interacts with a number of regulatory factors including REC114, MEI4 and IHO1. Despite the key role this process has in the continuation, and genetic variation, or eukaryotic life, there is very little known about how this process is regulated. Laroussi et al make use of biochemical, biophysical and structural biological approaches to extensively characterise the REC114-MEI4-IHO1 complex.

This is an outstanding biochemical paper. The experiments are well planned and beautifully executed. The protein purifications used are very clean, and the figures well presented. Importantly Laroussi et. al describe, and carefully characterise through point mutational analysis, the direct physical interaction between IHO1 and REC114-MEI4. This is an interaction that has, at least in yeast, previously been suggested to be driven by liquid-liquid separation. The careful and convincing work presented here represents an important paradigm-shift for the field.

I am fully supportive of publication of this excellent and important study.

Major comments:

My only major concern is regarding Figure 4, and specifically the AF2 model of the coiled-coil tetramer of IHO1. Given the ease with which MSAs of coiled-coils can become "contaminated" with non-orthologous sequences, I would urge some caution with this model. This is especially since the yeast ortholog of IHO1, Mer2, has been previously reported to be an anti-parallel tetramer (albeit, not very well supported by the data). The authors have several choices here. 1) They could simply reduce the visibility of the IHO1 tetramer model, and indicate caution in the parallel tetramer model. 2) They could consider using a structure prediction algorithm that doesn't use an MSA (e.g. ESMFold). 3) They could try to obtain experimental evidence for a parallel coiled-coil tetramer, e.g. through EM, SAXS or FRET approaches. I would like to make it crystal clear, however, that I would be very supportive of approach 1) or 2). An experimental approach is not necessary.

Assuming the authors don't take a wet-lab approach, this shouldn't take more than a couple of weeks.

Minor comments:

1. The observation that REC114 and MEI4 can also form a 4:2 complex is very interesting and potentially important. Did the authors also try to model this higher order complex in AF2?
2. Similarly to above, what does the prediction of the full-length REC114:MEI4 2:1 complex look like? Presumably the predicted interaction regions align well with experimental data, but it would be interesting to see (and easy to run).
3. Did the authors carry out SEC-MALS experiments on any IHO1 fragment lacking the coiled-coil domain? It was previously reported for Mer2 that the C-terminal region can form dimers, for example (OPTIONAL).
4. Given that full-length REC114 is used for the IHO1 interaction studies, do the authors have any data as to the stoichiometry of the REC114FL-MEI41-127 complex? (OPTIONAL)
5. Did the authors try AF2 modelling of the REC114-IHO1 interaction using orthologs from other species?

Referees cross commenting

I will add cross-comments to the comments of Reviewer #2

Firstly, the comments made by Reviewer #2 are technically correct. Firstly, reviewer #2 points out that the oligomerization states that the authors report could, in part, be artifactual the based on the his-tag purification method. This is indeed correct. However, given that none of the oligomerization states reported are per se unusual, given what is already known (including pre-prints from the Keeney and Claeys Bouuaert laboratories), I think the authors could forego this step.

Secondly, the use of an experimental structural method, such as SAXS, would certainly add value to the paper. Also Reviewer #2 is correct in pointing out the availability of the ESRF beamlines to the authors. However, while SAXS is a useful method, I personally consider the use of mutants to validate the interactions, an even stronger piece of evidence that the AlphaFold2 interactions are correct. I must disagree somewhat with Reviewer #2 with their argument that SAXS would validate the fold. Certainly if one of the AF2 predicted structures is radically wrong, then SAXS would produce scattering data, and a subsequent distance distribution plot that is incompatible with the AF2 model. However, a partly correct AF2 model, of roughly the right shape, might still fit into a SAXS envelope.

Reviewer #2 shares my concern on the parallel coiled-coil of IHO1, and their suggested solution is very elegant.

In my view, due to the time constraints imposed by the partially competing work from the the Keeney and Claeys Bouuaert laboratories (recently on biorxiv). I would support the authors if they chose the quickest route to publication.

Significance

General assessment: The strengths of the paper are as follows:

1. Quality of experiments - The proteins used have been properly purified (SEC) and properly handled. The experiments are carefully carried out and controlled.
2. Detail - The authors carry out the considerable effort of characterising protein interactions. through separation-of-function mutants. This adds to the quality of the paper, and renders the AF2 models as convincing as experimentally determined structures
3. Conceptual advances - The most important conceptual advance is the direct binding of the N-term of IHO1 to REC114. That this is the same region as used by both TOPOVIBL and ANKRD31 points to a complex regulation.
4. Integrity - the authors have taken great care not to "oversell" the results. The data are presented, and analysed, without hyperbole.

Limitations - The only limitation of the paper is the lack of in vivo experiments to test their findings. However given the time and effort required, and the pressing need to publish this exciting study, this is not a problem.

Advance: The paper provides advances from a number of directions, both conceptual and mechanistic. Mechanistically the description of the REC114-MEI14 complex is important, and in particular the observation that it can also form a higher order 4:2 structure. Likewise, while IHO1 was inferred to be a tetramer (based on work on Mer2) this was never proven formally. Most importantly, is the physical linkage between IHO1 and REC114, and that this is an interaction that is incompatible with TOPOVIBL and ANKRD31.

Audience: Given the central role of meiotic recombination in eukaryotic life, any studies that shed additional light on the regulation of meiosis are suitable for a broad audience. However, this subject paper will be more specifically of interest to the meiosis community. The elegant methodology will also be of interest to structural biologists and protein biochemists.

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Reply to the reviewers

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Reply to the reviewers

We sincerely thank the reviewers for their comprehensive and constructive feedback. Below, we submit our revision plan addressing the points raised by the reviewers.

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

The study analyzes the role of SLIT2 in clearance of S. aureus via neutrophils. It suggests that N-SLIT2 play a key role as an amplifier of the ROS response and release of antimicrobial peptides. The manuscript is well written and technologically sound. However, a few issues need to be addressed that preclude publication of the manuscript:

We thank the reviewer for the positive feedback.

Major comments:

1. The study analyzes different parameters of neutrophil function. One major effect of neutrophil activation is NETosis. This has not been addressed in the study albeit it is deemed to act in concert with the other immune mechanisms described.

We thank the reviewer for the suggestion. S. aureus is known to promote NET formation as well as to enhance NET degradation to increase bacterial survival in vivo (Meyers, Crescente et al., 2022, Thammavongsa, Missiakas et al., 2013). Several cellular kinases (Erk, Akt, p38) have been implicated in ROS-induced NETosis, but the exact role of p38 signaling in NETosis remains less clear (Douda, Khan et al., 2015). As recommended by the reviewers, we will now investigate whether N-SLIT2 regulates S. aureus-induced NETosis in neutrophils using Sytox Green, a membrane-impermeable nucleic acid label, as previously described (Douda et al., 2015).

Furthermore, the authors discuss a role of SLIT2 in the regulation of neutrophil migration. However, the current data set does not provide sufficient evidence for this. The reviewer suggests that the authors provide migration/chemotaxis assays and/or in vivo data to prove their hypothesis or revise their argumentation.

Several groups, including ours, have previously demonstrated that SLIT2-ROBO1 signaling potently inhibits neutrophil chemotaxis in vitro and in vivo. The in vivo models, in which the negative effects of SLIT2 on neutrophil migration have been shown, include mouse models of peritonitis (Tole, Mukovozov et al., 2009), allergic airway inflammation (Ye, Geng et al., 2010), renal ischemia-reperfusion injury (Chaturvedi, Yuen et al., 2013), and cholangiocarcinoma (Zhou, Luo et al., 2022). Additionally, a recent study showed that shRNA-mediated knockdown of SLIT2 resulted in increased neutrophil infiltration into murine tumors further supporting negative regulatory effect of SLIT2 on neutrophil migration (Geraldo, Xu et al., 2021). In the revised version of the manuscript, we will now discuss these important points in the Introduction and Discussion sections.

In our current study, in an effort to selectively examine the effects of SLIT2 on neutrophil function rather than on neutrophil migration, we intentionally administered N-ROBO1 to block endogenous SLIT2 signaling at 48 and 72 hours after inducing skin and soft tissue infection (SSTI) with S. aureus. In this model, the majority of neutrophil influx occurs early on, namely within 24 hours (Prabhakara, Foreman et al., 2013). We observed that blocking endogenous SLIT2 signaling in a murine model of SSTI resulted in enhanced localized infection and injury. We will now use immunohistochemical analysis to measure tissue infiltration of neutrophils (Ly6G+F4/80-) (Chadwick, Macdonald et al., 2021). In addition, as previously described we will also use IHC to evaluate within the tissue 8-hydroxydeoxyguanosine (8-OHdG), an indicator of oxidative damage (Sima, Aboodi et al., 2016). We will compare levels of 8-OHdG to the number of neutrophils in the tissue as a gross indicator of local ROS production by infiltrating neutrophils.

The timeline of SLIT2 expression indicates that environmental conditions could influence the expression of SLIT2. Have the authors analyzed whether SLIT2 expression is affected by low pH or hypoxia? Is there any data indicating what factors regulate SLIT2 expression? In the same line, it would be interesting to know whether SLIT2 immune effects (specifically ROS and LL37 release) are similarly triggered under hypoxic conditions often found in an abscess.

We thank the reviewer for raising this important point and for the suggestions. The regulation of SLIT2 levels in tissues is an active area of research. Hypoxia has been reported to increase SLIT2 expression in placental tissue (Liao, Laurent et al., 2012) but this has not been investigated in the context of bacterial infection. In different physiologic and pathophysiologic settings, vascular endothelial cells, including dermal microvascular endothelial cells (DMEC), have been shown to be an important source of SLIT2 (Romano, Manetti et al., 2018, Tavora, Mederer et al., 2020). We will therefore investigate the effects of hypoxia and low pH, conditions founds within bacterial abscesses, on production of SLIT2 by DMEC. DMEC will be infected with S. aureus and grown in normoxic and hypoxic (2% O2) conditions for up to 72 hours, the time-point at which maximal SLIT2 levels were detected in S. aureus-induced SSTI. We will collect cells and cultured supernatant for measurement of levels of Slit2 mRNA and SLIT2 protein at different time points ranging from 0 to 72 hours after infection. We will incubate neutrophils with the conditioned medium from hypoxic DMEC to measure the effect on LL-37 secretion. Finally, we will expose neutrophils to S. Aureus (+/- N-SLIT2) in a medium with pH ranging from 5.5 to 7.4 and then measure the LL-37 secretion as the reviewer suggested (Zhou & Fey, 2020).

Lastly, it is unclear whether SLIT2 binds to a defined target on the neutrophil. This needs to be highlighted in the discussion in respect to future work and ideally resolved experimentally.

We apologize for the confusion. We and others have previously demonstrated that human and murine neutrophils express ROBO1 but not ROBO2, and that ROBO1 is the primary Roundabout receptor which binds N-SLIT2 in immune cells (Rincon, Rocha-Gregg et al., 2018, Tole et al., 2009). We have now included this information in the Introduction section (please see page- 3). In our manuscript we showed experimentally that incubation of N-SLIT2 with the soluble N-terminal fragment of ROBO1 (N-ROBO1), which contains the N-SLIT2 binding Ig1 motif (Morlot, Thielens et al., 2007), blocked the effect of N-SLIT2 on ROS production, thereby confirming that the observed actions of SLIT2 occurred through ROBO1 (Fig. 1G). In the revised version of the manuscript, we will clarify this point.

Reviewer #1 (Significance (Required)):

The manuscript provides insight into a new mechanism regulating neutrophil function in the presence of S. aureus. The study provides evidence that the N-terminus of SLIT2 is involved in these effects and highlights p38-mediated signaling events as molecular targets increasing antibacterial effects in neutrophils. However, some contradictory findings imply that timing of the response is crucial.

Nevertheless, with the molecular mechanisms not fully understood many questions remain and the study adds to the complexity of the anti-staphylococcal immune response. Therefore, the audience for this manuscript requires knowledge on S. aureus-specific host-pathogen interaction and is not suitable for a broad audience as it does not provide information on a generally new mechanism of neutrophil activation or defense.

We thank the reviewer for pointing out the complexity of host-pathogen (neutrophils and S. aureus) interactions. SLIT2 is well-known for its anti-inflammatory properties via its effects on immune cell chemotaxis in vivo (Anand, Zhao et al., 2013, Chaturvedi et al., 2013, Geraldo et al., 2021). We demonstrated that SLIT2-ROBO1 signaling inhibits macropinocytosis in macrophages, and consequently, attenuates NOD2-induced inflammasome activation in mice (Bhosle, Mukherjee et al., 2020). Based on these earlier observations, SLIT2 would be anticipated to impair the innate immune response to infection. Unexpectedly, we found that SLIT2 does not impair, but instead enhances the ability of neutrophils to kill S. aureus. Indeed, through different mechanisms SLIT2 has been shown to have widespread anti-microbial properties against not only S. aureus but instead against diverse pathogens, including Mycobacterium tuberculosis, intestinal pathogens, H5N1 influenza, and most recently, COVID-19 (Gustafson, Ngai et al., 2022, London, Zhu et al., 2010). Together, these studies highlight the importance of spatiotemporal regulation of SLIT2 levels in tissues during bacterial and viral infection and the direct effects of SLIT2 on modulating host-pathogen interactions.

Additionally, SLIT2-induced p38 MAPK activation is not limited to innate immune cells. Li et al. reported this week that SLIT2-ROBO1 signaling activates p38 in pancreatic ductal adenocarcinoma cells as well as metastatic tumors (Li, Zhang et al., 2023). In the revised manuscript, we will discuss all of the important points above.

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

Summary: The manuscript deals with the role of the neurorepellent SLIT2 in killing of the bacterial pathogen Staphylococcus aureus. The authors show that neutrophils incubated with the N-terminal region of SLIT2 kill S. aureus more efficiently than neutrophils without pre-exposure to N-SLIT2. This effect was due to an increased production of reactive oxygen species by NADPH oxidase complex activation and stimulating exocytosis of antibacterial peptide containing granules. The concept was proven in an animal model of skin and soft tissue infection in mice in which neutralization of endogenous SLIT2 reduced CFU numbers in ear skin and decreased tissue destruction in response to S. aureus infection.

Major comments:

1. In general the findings and key conclusions are convincingly covered by the results presented in the manuscript. The methods are adequate to allow the conclusions drawn. Data are clearly presented and easy to follow. Statistical methods are appropriate.

We thank the reviewer for the positive feedback. In the present study, we investigated the effects of SLIT2 on NADPH oxidase (NOX – p47phox) priming. Using novel methodology, neutrophil priming was recently shown to be associated with characteristic cytoskeletal changes (Bashant, Vassallo et al., 2019). We are now collaborating with Dr. Nicole Toepfner (Technische Universität Dresden, Dresden) to investigate SLIT2-induced cytoskeletal changes in neutrophils isolated from whole blood using Real-time deformability cytometry (RT-DC). We believe that these novel studies will further enhance the revised manuscript.

Minor comments:

1. In the Materials and Methods section line 340 a GFP-expressing S. aureus USA300 strain is indicated. What was the exact strain designation, e.g. LAC or JE2, as USA300 is not a strain name (different strains belong to this pulsed-field electrophoresis based classification).

We thank the reviewer for this comment. The strain designation of the GFP-expressing S. aureus we used is USA300 LAC (Flannagan, Kuiack et al., 2018). In the revised version of the manuscript we will include the correct information (please see page- 10).

In the legend of figure 3 the inhibitors are mentioned for part B and E but not C and D.

We apologize for the error. Figure 3 legend has now been corrected in the revised manuscript.

Figure S4 would be nice to have in the main manuscript.

We thank the reviewer for the suggestion. In the revised manuscript we moved original Supplementary Fig. S4B to main Fig. 4B in the manuscript. The schematic from main Fig. 4B is moved to the new Supplementary Fig. 4B. The graphical summary (original Supplementary Fig. S4C) is now presented as new main Figure 5.

Reviewer #2 (Significance (Required)):

The manuscript deals with a novel mechanism of neutrophil activation by SLIT-2, a protein which was originally thought to act in the nervous system but is also expressed in many peripheral tissues. Importantly SLIT-2 may be involved in tumor suppression but also chemotaxis of immune cells. In this manuscript a novel, rather unexpected role of the N-terminal region of SLIT-2 in activation of antibacterial mechanisms of neutrophils was shown. This could be interesting for a broader readership interested in innate immune mechanisms and bacterial infections. Since little is known on the role of SLIT-2 in response to bacterial infections the paper could initiate a number of new studies in this field. This reviewer has experience with S. aureus virulence and resistance mechanisms and animal infection models.

We thank the reviewer for the very positive feedback regarding the appeal of our manuscript to a broad readership. As noted in our response to Reviewer #1 Significance, recent studies suggest that SLIT2 could not only serve as a therapeutic to combat S. aureus, but could have broad anti-microbial activity against a number of pathogens including Mycobacterium tuberculosis, intestinal pathogens, H5N1 influenza, and COVID-19 (Borbora, Bhatt et al., 2022, Gustafson et al., 2022, London et al., 2010). We believe that the ability of SLIT2 to combat diverse bacterial and viral infections will even further enhance the appeal of our manuscript to a broad audience. In the revised manuscript we will expand the discussion to include these very important points.

References:

Anand AR, Zhao H, Nagaraja T, Robinson LA, Ganju RK (2013) N-terminal Slit2 inhibits HIV-1 replication by regulating the actin cytoskeleton. Retrovirology 10: 2

Bashant KR, Vassallo A, Herold C, Berner R, Menschner L, Subburayalu J, Kaplan MJ, Summers C, Guck J, Chilvers ER, Toepfner N (2019) Real-time deformability cytometry reveals sequential contraction and expansion during neutrophil priming. J Leukoc Biol 105: 1143-1153

Bhosle VK, Mukherjee T, Huang YW, Patel S, Pang BWF, Liu GY, Glogauer M, Wu JY, Philpott DJ, Grinstein S, Robinson LA (2020) SLIT2/ROBO1-signaling inhibits macropinocytosis by opposing cortical cytoskeletal remodeling. Nat Commun 11: 4112

Borbora SM, Bhatt S, Balaji KN (2022) Mycobacterium tuberculosis infection elevates SLIT2 expression to modulate oxidative stress responses in macrophages. bioRxiv: 2022.10.13.512188

Chadwick JW, Macdonald R, Ali AA, Glogauer M, Magalhaes MA (2021) TNFalpha Signaling Is Increased in Progressing Oral Potentially Malignant Disorders and Regulates Malignant Transformation in an Oral Carcinogenesis Model. Front Oncol 11: 741013

Chaturvedi S, Yuen DA, Bajwa A, Huang YW, Sokollik C, Huang L, Lam GY, Tole S, Liu GY, Pan J, Chan L, Sokolskyy Y, Puthia M, Godaly G, John R, Wang C, Lee WL, Brumell JH, Okusa MD, Robinson LA (2013) Slit2 prevents neutrophil recruitment and renal ischemia-reperfusion injury. J Am Soc Nephrol 24: 1274-87

Douda DN, Khan MA, Grasemann H, Palaniyar N (2015) SK3 channel and mitochondrial ROS mediate NADPH oxidase-independent NETosis induced by calcium influx. Proc Natl Acad Sci U S A 112: 2817-22

Flannagan RS, Kuiack RC, McGavin MJ, Heinrichs DE (2018) Staphylococcus aureus Uses the GraXRS Regulatory System To Sense and Adapt to the Acidified Phagolysosome in Macrophages. mBio 9

Geraldo LH, Xu Y, Jacob L, Pibouin-Fragner L, Rao R, Maissa N, Verreault M, Lemaire N, Knosp C, Lesaffre C, Daubon T, Dejaegher J, Solie L, Rudewicz J, Viel T, Tavitian B, De Vleeschouwer S, Sanson M, Bikfalvi A, Idbaih A et al. (2021) SLIT2/ROBO signaling in tumor-associated microglia and macrophages drives glioblastoma immunosuppression and vascular dysmorphia. J Clin Invest 131

Gustafson D, Ngai M, Wu R, Hou H, Schoffel AC, Erice C, Mandla S, Billia F, Wilson MD, Radisic M, Fan E, Trahtemberg U, Baker A, McIntosh C, Fan CS, Dos Santos CC, Kain KC, Hanneman K, Thavendiranathan P, Fish JE et al. (2022) Cardiovascular signatures of COVID-19 predict mortality and identify barrier stabilizing therapies. EBioMedicine 78: 103982

Li Q, Zhang XX, Hu LP, Ni B, Li DX, Wang X, Jiang SH, Li H, Yang MW, Jiang YS, Xu CJ, Zhang XL, Zhang YL, Huang PQ, Yang Q, Zhou Y, Gu JR, Xiao GG, Sun YW, Li J et al. (2023) Coadaptation fostered by the SLIT2-ROBO1 axis facilitates liver metastasis of pancreatic ductal adenocarcinoma. Nat Commun 14: 861

Liao WX, Laurent LC, Agent S, Hodges J, Chen DB (2012) Human placental expression of SLIT/ROBO signaling cues: effects of preeclampsia and hypoxia. Biol Reprod 86: 111

London NR, Zhu W, Bozza FA, Smith MC, Greif DM, Sorensen LK, Chen L, Kaminoh Y, Chan AC, Passi SF, Day CW, Barnard DL, Zimmerman GA, Krasnow MA, Li DY (2010) Targeting Robo4-dependent Slit signaling to survive the cytokine storm in sepsis and influenza. Sci Transl Med 2: 23ra19

Meyers S, Crescente M, Verhamme P, Martinod K (2022) Staphylococcus aureus and Neutrophil Extracellular Traps: The Master Manipulator Meets Its Match in Immunothrombosis. Arterioscler Thromb Vasc Biol 42: 261-276

Morlot C, Thielens NM, Ravelli RB, Hemrika W, Romijn RA, Gros P, Cusack S, McCarthy AA (2007) Structural insights into the Slit-Robo complex. Proc Natl Acad Sci U S A 104: 14923-8

Prabhakara R, Foreman O, De Pascalis R, Lee GM, Plaut RD, Kim SY, Stibitz S, Elkins KL, Merkel TJ (2013) Epicutaneous model of community-acquired Staphylococcus aureus skin infections. Infect Immun 81: 1306-15

Rincon E, Rocha-Gregg BL, Collins SR (2018) A map of gene expression in neutrophil-like cell lines. BMC Genomics 19: 573

Romano E, Manetti M, Rosa I, Fioretto BS, Ibba-Manneschi L, Matucci-Cerinic M, Guiducci S (2018) Slit2/Robo4 axis may contribute to endothelial cell dysfunction and angiogenesis disturbance in systemic sclerosis. Ann Rheum Dis 77: 1665-1674

Sima C, Aboodi GM, Lakschevitz FS, Sun C, Goldberg MB, Glogauer M (2016) Nuclear Factor Erythroid 2-Related Factor 2 Down-Regulation in Oral Neutrophils Is Associated with Periodontal Oxidative Damage and Severe Chronic Periodontitis. Am J Pathol 186: 1417-26

Tavora B, Mederer T, Wessel KJ, Ruffing S, Sadjadi M, Missmahl M, Ostendorf BN, Liu X, Kim JY, Olsen O, Welm AL, Goodarzi H, Tavazoie SF (2020) Tumoural activation of TLR3-SLIT2 axis in endothelium drives metastasis. Nature 586: 299-304

Thammavongsa V, Missiakas DM, Schneewind O (2013) Staphylococcus aureus degrades neutrophil extracellular traps to promote immune cell death. Science 342: 863-6

Tole S, Mukovozov IM, Huang YW, Magalhaes MA, Yan M, Crow MR, Liu GY, Sun CX, Durocher Y, Glogauer M, Robinson LA (2009) The axonal repellent, Slit2, inhibits directional migration of circulating neutrophils. J Leukoc Biol 86: 1403-15

Ye BQ, Geng ZH, Ma L, Geng JG (2010) Slit2 regulates attractive eosinophil and repulsive neutrophil chemotaxis through differential srGAP1 expression during lung inflammation. J Immunol 185: 6294-305

Zhou C, Fey PD (2020) The acid response network of Staphylococcus aureus. Curr Opin Microbiol 55: 67-73

Zhou SL, Luo CB, Song CL, Zhou ZJ, Xin HY, Hu ZQ, Sun RQ, Fan J, Zhou J (2022) Genomic evolution and the impact of SLIT2 mutation in relapsed intrahepatic cholangiocarcinoma. Hepatology 75: 831-846

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Referee #2

Evidence, reproducibility and clarity

Summary:

The manuscript deals with the role of the neurorepellent SLIT2 in killing of the bacterial pathogen Staphylococcus aureus. The authors show that neutrophils incubated with the N-terminal region of SLIT2 kill S. aureus more efficiently than neutrophils without preexposure to N-SLIT2. This effect was due to an increased production of reactive oxygen species by NADPH oxidase complex activation and stimulating exocytosis of antibacterial peptide containing granules. The concept was proven in an animal model of skin and soft tissue infection in mice in which neutralization of endogenous SLIT2 reduced CFU numbers in ear skin and decreased tissue destruction in response to S. aureus infection.

Major comments:

In general the findings and key conclusions are convincingly covered by the results presented in the manuscript. The methods are adequate to allow the conclusions drawn. Data are clearly presented and easy to follow. Statistical methods are appropriate.

Minor comments:

In the Materials and methods section line 340 a GFP-expressing S. aureus USA300 strain is indicated. What was the exact strain designation, e.g. LAC or JE2, as USA300 is not a strain name (different strains belong to this pulsed-field electrophoresis based classification). In the legend of figure 3 the inhibitors are mentioned for part B and E but not C and D. Figure S4 would be nice to have in the main manuscript.

Significance

The manuscript deals with a novel mechanism of neutrophil activation by SLIT-2, a protein which was originally thought to act in the nervous system but is also expressed in many peripheral tissues. Importantly SLIT-2 may be involved in tumor suppression but also chemotaxis of immune cells. In this manuscript a novel, rather unexpected role of the N-terminal region of SLIT-2 in activation of antibacterial mechanisms of neutrophils was shown. This could be interesting for a broader readership interested in innate immune mechanisms and bacterial infections. Since little is known on the role of SLIT-2 in response to bacterial infections the paper could initiate a number of new studies in this field.

This reviewer has experience with S. aureus virulence and resistance mechanisms and animal infection models.

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 study analyzes the role of SLIT2 in clearance of S. aureus via neutrophils. I suggests that N-SLIT2 play a key role as an amplifier of the ROS response and release of antimicrobial peptides. The manuscript is well written and technologically sound. However, a few issues need to be addressed that preclude publication of the manuscript:

Major comments

The study analyzes different parameters of neutrophil function. One major effect of neutrophil activation is NETosis. This has not been addressed in the study albeit it is deemed to act in concert with the other immune mechanisms described.

Furthermore, the authors discuss a role of SLIT2 in the regulation of neutrophil migration. However, the current data set does not provide sufficient evidence for this. The reviewer suggests that the auhtors provide migration/chemotaxis assays and/or in vivo data to prove their hypothesis or revise their argumentation. The timeline of SLIT2 expression indicates that environmental conditions could influence the expression of SLIT2. Have the authors analyzed whether SLIT2 expression is affected by low pH or hypoxia? Is there any data indicating what factors regulate SLIT2 expression?

In the same line, it would be interesting to know whether SLIT2 immune effects (specifically ROS and LL37 release) are similarly triggered under hypoxic conditions often found in an abscess? Lastly, it is unclear whether SLIT2 binds to a defined target on the neutrophil. This needs to be highlighted in the discussion in respect to future work and ideally resolved experimentally.

Significance

The manuscript provides inisght into a new mechanism regulating neutrophil function in the presence of S. aureus. The study provides evidence that the N-terminus of SLIT2 is involved in these effects and highlights p38-mediated signaling events as molecular targets increasing antibacterial effects in neutrophils. However, some contradictory findings imply that timing of the response is crucial. Nevertheless, with the molecular mechanisms not fully understood many questions remain and the study adds to the complexity of the antistaphyloccocal immune response. Therefore, the audience forthis manuscript requires knowledge on S. aureus-specific host-pathogen interaction and is not suitable for a broad audience as it does not provide information on a generally new mechanism of neutrophil activation or defense.

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Reply to the reviewers

We thank the reviewer for their comments. We are encouraged that the reviewers found our research “important study that addresses the interplay between two major Rho-type small GTPases involved in cell division” and “of interest to those interested in the cell biology of mitotic exit”. We agree with the comments raised by the reviewers and have provided new data as per their recommendation. We have also made changes to the text and format of the paper. We feel that with these changes the manuscript is stronger and we thank the reviewers for their suggestions. Below we provide a detailed response to the reviewers’ comments.

Reviewer #1

*This manuscript focuses on the role of Cdc42 in Rho1 activation during fission yeast cytokinesis. The primary finding is that active Cdc42 and its downstream effector Pak1 prevents accumulation of active Rho1 and the synthesis of cell wall material, at early stages of cytokinesis and despite the local recruitment of the Rho1 GEF Rgf1. The data supporting these conclusions are reasonably sound. *

*Additional experiments are presented to suggest that Cdc42 and Pak1 negatively regulate Rgf1, this conclusion is not as strongly supported (though it may be true) *

*These study relies on a newly described probe for active Rho1. However this probe is not sufficiently well validated. *

*Overall the manuscript was not assembled with sufficient care and rigor, these deficits could be readily corrected. *

The major point of the paper is that Cdc42 and Pak1 negatively regulate Rho1 activation. However, during late cytokinesis, active Cdc42 and active Rho1 co-exist at the division site. Thus, Cdc42 activation induces a delay in Rho1 activation, but how this delay is overcome is not investigated or even discussed. Indeed, while the delay is shown the transience of this inhibition is not explicitly mentioned. At a minimum, the authors should highlight this point for the readers.

We are encouraged by the fact that the reviewer found our data “reasonably sound”. We agree that this manuscript does not provide the molecular details of how Cdc42 inhibits Rho1 activation. Our genetic data suggests that this is likely mediated by multiple pathways possibly involving the regulation of the Rho regulators Rgf1, Rgf2 and Rga5. We are currently investigating the molecular details of this regulation and hope to report it in another manuscript.

Our data shows that while Cdc42 inhibits Rho1, the SIN pathway is essential for Rho1 activation regardless of the presence of Cdc42. While Cdc42 is activated at the division site as the ring completes assembly, the SIN pathway is activated immediately prior to ring constriction similar to that of Rho1 activation. It is possible that once the SIN is activated at the division site, it overcomes Cdc42-mediated Rho1 inhibition. We have highlighted this in the discussion section of this manuscript and are currently investigating the molecular details of this regulation.

*Specific points 1 - RBD probe This probe is central to this manuscript. However, there is insufficient validation of its target. Figure 1 shows the localization and its independence of Rho2. The authors should provide direct evidence that it recognizes Rho1 (for example using a repressible promotor or an anchor away approach).

*

We thank the reviewers for their comments on the RBD probe. We have now provided validation for the RBD-probe. We have used rho1 temperature-sensitive and switch-off mutants to show loss of RBD-probe localization in these mutants. This data is provided I the revised manuscript in Fig1 and Supplementary fig. S1.

At various places in the manuscript the authors refer to this probe as "Rho-probe", RBD-probe, RBD, RBD-(mNG or tdTomato). On page 11 the authors state, "As per our observations, we refer to the Rho-probe signal at the division site as active Rho1 from here onwards." Yet, in the very next paragraph they refer to the localization of the "Rho probe". * This is also an issue with the figures. For example, in figures 4B,C ; 5B,C; 6B; 7B,C the figures are titled either "Rho1 activation at division site", "Rho1-probe at division site"; "Rho1-probe appearance at division site" ; "Rho1-probe in non-constricting rings". *

We agree that these multiple terms to describe the probe is confusing. We have restricted the terms to either “RBD-mNG” or “RBD-tdTomato” when reporting the data and use “Rho-probe” for descriptive purposes.

In fig 3, RBD-nNG is quantified in a graph entitled "localizaton [sic] of Rho1-GEFs at division site"

We thank our reviewers for identifying this error in our labeling of the graph in Fig. 3E. This figure now reads “Localization of Rgf1, Rgf3, active Rho1 at the division site”

In all figures but two, 5c and 7c, the authors quantify Rho1 activation by the presence or absence of the probe, rather than a quantitative measure or the extent of recruitment of the probe. This could be analyzed my quantitatively.

We appreciate this comment and provide this response in order to clarify our reasoning for presenting this data. We quantified the intensities of RBD-mNG or RBD-tdTomato where ever relevant to the question we are addressing for each experiment performed.

Where we look at Rho1 activation at the division site with respect to SPB distances, we are reporting the differences in the timing of Rho activation with respect to mitotic progression. However, in Figures 5c and 7c, and now also Fig 1 of the revised manuscript, we quantified the intensities of the probe as this indicated the changes in overall active Rho1 levels under our experimental conditions. We have added in the text for earlier experiments where we do not report intensity measurements for the active Rho probe that we do not observe any differences in the intensity levels.

*2 - Regulation of Rgf1 by Cdc42 and Pak1. The results shown in figure 8 show that "early Rho1 activation in gef1 mutants is not Rgf3-dependent". Figure 9 establishes "loss of rgf1 prevents premature Rho1 activation in gef1Δ cells restoring it to normal in late anaphase (Fig.9A, B)." This finding indicates that Rgf1, but not Rgf3, is required for Rho1 premature activation. This finding doesn't rule out the possibility that Cdc42 and Pak1 might be required to turn off RhoGAPs to allow active Rho1 to accumulate. This analysis concludes with this unclear and ungrammatical sentence, "While we were unable to assess the Rho-probe in the rgf1Δ rgf2Δ double mutants due to its lethality [sic; is the Rho probe lethal?], our observations suggest that apart from Rgf1 early Rho1 activation in gef1Δ cells is either due to activation of Rgf2 or due to inhibition of Rga5." *

We thank you for your insight and agree with these remarks. We could not investigate Rho1 activation in rgf1Δ rgf2Δ double mutants since the double mutants are inviable. We have re-worded the sentence to reflect our findings appropriately.

*The conclusion that this regulation is due to control of Rgf1 should be toned down. E.g. from the abstract: "We provide functional and genetic evidence which indicates that Pak1 regulates Rho1 activation likely via the regulation of its GEF Rgf1." *

We have now removed this statement from the abstract. We have also clarified in the discussion that the molecular details of how Cdc42 inhibits Rho1 is not known and needs to be investigated. While our data suggests that the regulator Rgf1 and Rga5 may be involved in the process the details are unclear and we are currently investigating this regulation.

*SECTION B - Significance ======================== This manuscript ties together several recent papers from the author's lab on the control of Cdc42 activation during cytokinesis and older papers on the role of Rho1 in Bgs1 activation. It provides missing information into the temporal regulation of septum assembly.

The authors make a point of the similarities of fission yeast cytokinesis to animal cell cytokinesis. Indeed the second sentence reads, "The fission yeast model system divides via an actomyosin-based contractile ring, which is assembled in the medial region of the cell, as in animal cells (Balasubramanian et al., 2004; Pollard, 2010).". However, the authors fail to point out the many differences between yeast and animal cell cytokinesis until the last paragraph of the discussion. If the authors want to include the similarities in the introduction, they should also include the differences. For example, ring assembly is independent of Rho1 activation in fission yeast, but dependent on RhoA activation in animal cells. *

We thank the reviewer for pointing out this deficiency in our writing. We have now amended the introduction to highlight the differences between Rho1 activity in fission yeast and animal cells during cytokinesis. We have added the following text to the Introduction section.

“The animal Rho1 homolog RhoA is required for ring formation and is essential for cytokinesis (Basant and Glotzer, 2018). While in yeast, Rho1 is essential for septum formation, the current literature suggests that it is dispensable for ring formation (Onishi et al., 2013; Yoshida, 2009). In fission yeast where both the actomyosin ring and the septum have important roles in the proper coordination of cytokinesis, Rho1 has no reported roles in ring formation but is essential for septation (Balasubramanian et al., 2004).”

*This work will be of interest to biologists working on yeast cell division. To a lesser extent it will be of interest to biologists interested in cytokinesis and coordination of distinct GTPase pathways.

Additional points*

1 - The text is overly wordy and needs extensive revision. Many of the experiments could be explained more clearly and with somewhat less genetic jargon. The introduction has quite a bit of extraneous information and lacks relevant facts, such as the function of Bgs1, which is central to the results.

We have now modified the text to remove unnecessary genetic jargon. We have also provided additional text to describe the role of Bgs1 in the Introduction.

2 - page 4 "GEFs promote GTP binding, thus keeping the GTPase active while the GAPs increase GTP hydrolysis, thus promoting GTPase inactivation." GEFs promote GTP binding, but they do not keep the GTPase active (an inhibitor of a RhoGAP would do that), they activate the GTPases.

We thank the reviewers for highlighting this error. We have corrected this sentence, which now reads “GEFs promote GTP exchange to activate the GTPase, while the GAPs increase GTP hydrolysis to promote GTPase inactivation.”

*3 - The current literature on animal cell cytokinesis indicates little direct role in cytokinesis, rather than the author's statement, "In larger eukaryotes, the role of Cdc42 activation has been reported mostly in meiotic division events such as polar body extrusion in oocytes, but not much is known about its role in cytokinesis in somatic cell division (Drechsel et al., 1997; Na and Zernicka-Goetz, 2006)." See for example, PMID 10898977, 10871280 which indicate Cdc42 does not play a major role during cytokinesis in at least a few systems where it has been analyzed. *

We thank our reviewer for this observation and agree that this statement can be expanded to further explain the role of Cdc42 in animal cytokinesis. The paragraph has been re-written as follows-

Pg5 - “In animal cells, the direct role of Cdc42 in cytokinesis remains indefinite. In Xenopus embryos and mouse fibroblasts for example, constitutively active Cdc42 impairs cytokinesis completion (Drechsel et al., 1997). However, in other cases such as in mouse embryonic stem cells, Cdc42 was only critical for development but not cytokinesis (Chen et al., 2000). RNA interference in animal cells demonstrate that that while RhoA is required for cytokinesis, Cdc42 is not required for this process (Jantsch-Plunger et al., 2000). Cdc42 also promotes spindle positioning and polar body extrusion in mouse oocytes, but it is not known whether its localization at these spindles affects RhoA (Na and Zernicka-Goetz, 2006). Thus, the role of Cdc42 in the cytokinetic process may be cell-type specific, and these data highlight the importance for more investigation to elucidate Cdc42 regulation in dividing cells (Jordan and Canman, 2012).”

Reviewer #2

*In many fungal cells, including fission yeast, the deposition of a new cell wall (a septum) between daughter cells is essential for cytokinesis. Cell wall synthases are trafficked to and activated at the division site, and dysregulated trafficking and/or synthase activation can lead to cytokinetic defects. In this study, the authors use fluorescent probes for Cdc42 and Rho1 activity and live-cell imaging to investigate the timing and regulation of Rho1 activity in fission yeast, and specifically, the role of Cdc42 in regulating Rho1. Summary of the proposed model: Gef1 -> active Cdc42 -> Pak1 --| Rgf1 -> active Rho1 -> septum formation

Major comments

(1) As far as I can gather from the authors' description in the manuscript and quick literature search, this will be the first publication in S. pombe utilizing the HR1-C2 domain of Pkc2p as fluorescent probe for active Rho1 (RBD-mNG). While a comparable domain of S. cerevisiae Pkc1p (not "pck2" as referenced by the authors in Page 25) has been used for similar purposes, given the importance of this probe and the precedent it sets in the S. pombe literature, it is imperative that proper tests are performed to validate that its localization reflects activity of Rho1 and nothing else (such as membrane binding of the C2 domain or transcriptional regulation of the pkc2 promoter). Such tests should also be independent of the hypotheses central to the current study (i.e., effects of Gef1, Pak1, Rgf1/2 on the timing of RBD-mNG localization). Can the authors provide data to address this point? Examples include, but not limited to, rho1 mutants, expression of constitutively active Rho1, or temporary expression of dominant-negative Rho1.*

We agree with the reviewer and now provide data to show loss of the localization of the Rho-probe RBD-mNG in rho1 mutants. Using temperature-sensitive and switch-off mutants we show that under mutant conditions the RBD-mNG localization is lost at the division site and also from the cell ends. This provides strong evidence that the probe detects active Rho1 in the cells.

*(2) Related, M&M does not provide sufficient details about the amino-acid positions corresponding to the "RBD" domain of Pkc2, thus precluding readers from reproducing the experiments. This needs to be clarified. *

We now provide in the materials and methods the details of how this probe was generated including the base pairs of the budding yeast PKC1 and the fission yeast pck2 promoter.

(3) In Figure 1B, RBD1-mNG localizes clearly to the medial region of rho2∆ cells when the Rlc1-tdTomato ring has not formed. Does this mean that Rho2 has a major role in forming the contractile ring that is independent of Rho1 activation? On this other hand, however, data in Fig. S2BC suggest that RBD-mNG does not localize to the medial region in rho2∆ cells until Rlc1-tdTomato ring forms (the timing of which seems normal). This discrepancy needs to be addressed.

In response to the issue raised here, we do not see active Rho1 at the division site of cells without rings. However, after cytokinesis, while cells are in septation, although the ring has disappeared, active Rho1 lingers at the division site. The cell shown in the panel is a septated cell after ring constriction completes. We have included DIC panels of these cells to show that active Rho1 lingers in septating cells.

*(4) Given the nature of RBD-mNG localization, it seems unavoidable to have some level of arbitrariness in measuring the onset of its localization at the division site. It would be advisable for the authors to be specific in M&M about how they defined the onset of localization, i.e., whether it was based on universal threshold in signal intensity, ratio, etc. or on manual curation (ideally double-blind).

*

We have updated the methods to describe that “onset of localization” was performed via double-blind visual observations.

Minor comments (1) Throughout the manuscript, there are quite a few places where inconsistencies in genetic nomenclature can cause confusion to readers. Below are some examples. Figs. 6B, 7B, 10B: pak1(-ts), shk1, and orb2-34 (including faint labels under category marks in 6B). Fig. 9B (gef1+ rgf1∆) vs 9C (rgf1∆). Wild-type alleles are implicit in some figures, while explicit in others.

We have corrected these inconsistencies.

*(2) The first hypothesis (Fig. 1C) is that the AMR might regulate Rho1 activation. The ring is disrupted with LatA, but Rho remains active. They cite this as evidence that the AMR does not activate Rho1, but were the cells treated before or after the rings formed? If before, then the experiment demonstrates what the authors claim, but if after, it only shows that the AMR is not essential to maintain Rho activity. *

We agree with the reviewer that this is an important distinction. We have modified this statement to “These results indicate that while at the division site the actin cytoskeleton is not required for maintaining Rho1 activation, it is necessary at the growth sites of interphase cells.”

*(3) Page 8: "Time-lapse imaging of cells simultaneously expressing CRIB-3xGFP and RBD-tdTomato [...] while Rho1 is activated ~20 minutes after SPB duplication (Fig. 2B)." This appears to refer to Fig. 2C. *

We thank the reviewers for catching this error in the text. We have now corrected it, showing timelapse as Fig. 2C, and an Image of cells simultaneously expressing CRIB and RBD as Fig. 2B.

*(4) Page 9: "[...] Rgf1 and Rgf3 localize as early as the time of ring assembly at an average SPB distance of 4-5 µm (Fig. 3D)." This sentence is confusing. How was the average calculated over the earliest ring assembly in non-time-lapse data? Fig. 3DE show distances between SPBs as short as 2.5 µm, not 4-5 µm, and average of ~8 µm for all cells at different stages of mitosis. This confusion needs to be clarified. *

We thank the reviewer for observing this mistake in our writing and interpretation. We agree that the text does not reflect the accurate interpretations of the data collected and have now fixed these errors. The current sentence reading “In an asynchronous population of cells, we find that Rgf1 and Rgf3 localize as early as the time of ring assembly at an average SPB distance of 4-5µm.” has now been replaced with the description shown below-

“Using the distance between SPBs of anaphase cells as a proxy for timing of cytokinesis, we find that in most anaphase cells, Rgf1-GFP and Rgf3-eGFP was localized at the division site at very early stages in anaphase (Fig. 3D, E). This can be observed by the short distance between the SPBs of ~2µm (Fig. 3D). We also measured the distance for which active Rho1 appeared at the division site, and find that at the distance between SPBs of ~10µm, active Rho1 was present at the division site in ~50% of the population of control cells (Fig. 3E).”

*(5) Fig. 5. Both the intensity and onset of RBD-mNG localization were affected by cdc42g12v expression. These two may form a causative relationship: reduced overall RBD signal may cause failed detection of early RBD localization. Can the authors compare cells with similar mean RBD-mNG signal intensities (Fig. 5B) and confirm that the timing of appearance at the division site is still delayed in gef1+ cdc42g12v relative to gef1+ empty? *

We thank the reviewers for pointing this out and appreciate the opportunity to further clarify our observations. While there is clear decrease in Rho-probe intensity at the division site of on cells expressing cdc42G12V, we did see some variation in the extent of the decrease likely due to the variation in the expression levels of cdc42g12V. To provide a more accurate analysis of our observation we have shown the changes in the timing and intensities of Rho-probe localization. However, due to the noisy nature of the data we cannot compare the intensities in individual cells at specific spindle pole body distance between cells. As observed cdc42G12V significantly reduces Rho1 activity globally, not just at the division site. To cherry-pick cdc42G12V cells with similar active rho1 intensity to assess time of Rho1 activation may lead to subconscious data manipulation and will not address how early Rho1 activation is regulated.

*Reviewer #3

Onwubiko et al., present a clear and well written manuscript detailing the mechanistic understanding of how Rho1 is activated in a timely manner to ensure cytokinesis occurs in a scheduled manner at the end of telophase. Using fission yeast as a model system, and with the development of a novel Rho1 biosensor, they implicate a series of GTPases, exchange factors, GTPase activating proteins and kinases acting downstream of Cdc42 in the timely activation of Rho1. Specifically, they find that Cdc42 prevents premature Rho1 activation in early anaphase in a manner requiring the kinase Pak1. They observe that the Rho1 activators Rgf1 and Rgf3 localise to the division site in early anaphase, but Rho1 doesn't get activated until late anaphase, suggesting that control mechanisms ensure that these GEFs are held inactive, or that RhoGAP activity is able to balance this activation in early anaphase. This suppression of Rho1 activity in early anaphase requires Cdc42 and Pak1 and implicate (by omission) Rgf1, rather than Rgf3, is the relevant GEF.

I liked this manuscript, it was clearly written the experimental progression was logical and the data were easy to interpret from the figures. The conclusions were precise, believable and not overstated. The manuscript provides novel observations and through good use of a series of rescues/mutants, illuminates a pathway that is held in check by Cdc42 to ensure timely Rho1 activation. The novel Rho1 probe is exciting and shows well differently regulated pools of active Rho1 at the division site and the growing tips. I thought the co-imaging/measurement of ring placement and SBP duplication allowed a really clear understanding of the kinetics during this rapid phase of the cell cycle. A critique of the study is that the the mechanism by which Cdc42 controls Pak1, and by which Pak1 controls Rgf1/Rgf2 is left unclear. I guess there could always be a molecular expansion of these points (e.g., how does Cdc42 control Pak1; how does Pak1 control Rgf1; how is Rgf activity restricted when localised), but I think that would only enhance, rather than change, the level of detail of the paper's message. I think the paper's current conclusions stand on their own, the data is clear and believable, the experiments are well performed. There are a number of observations in the paper that are left open for future studies, and I think this is a positive (e.g., any separable role of Rgf1/Rgf2 and how Rga5 integrates into this pathway. As such, I am tempted to recommend accept with only minor amendments as outlined below.

1. P8 P15: should the call out be to Fig 2C, rather than 2B. *

We thank reviewer for their highlighting this error in our text. We have now fixed it.

*P14 L17: should it be 'gef1+ rgf3-', not 'gef1+, rgf3+' *

We have fixed this error and further clarified the terms for easy understanding.

Structure wise, I thought the section on Rga5 didn't really fit well on P16; it seemed sandwiched between two sections on GEFs. Is there a more appropriate place to place these data - perhaps between the paragraph breaks on P17? Related to this data, the conclusion on P16 suggests 'other' regulators of RhoGAP activity act to repress Rho1 function. Would 'additional' regulators of RhoGAP activity be more appropriate as there is some function contributed by Rga5?

We have now moved this section to the end of the section on Rho1 regulators after we discuss the Rho1 GEFs. We have also modified the text to clarify that multiple regulators are likely involved in the regulation of Cdc42-mediated Rho1 inhibition.

*In Fig 10b, you haven't defined orb2-34. Is it the rgf1-delete?

*

The mutant orb2-34 is a temperature sensitive allele of the pak1 kinase. To avoid confusion, we have replaced the allele name with pak1-ts in figure 10 and in the text.

• I find the sentence at the top of P18: 'Rho1 activation in pak1+ rgf1+....at 25oC and 35.5oc occurred at longer and similar SBP distances' quite hard to interpret. Could you perhaps expand it to make your message clearer? *

We thank the reviewer for pointing this out. These statements have now been re-written for clarity. 'Rho1 activation in pak1+ rgf1+....at 25ºC and 35.5ºC” has been changed, and now reads as follows:

“The timing of RBD-mNG localization at the division site occurs late in cytokinesis during late anaphase as depicted by longer SPB distances in pak1+ rgf1+, pak1-ts rgf1+, and pak1+ rgf1Δ cells at 25ºC (Fig.10B). As previously shown, RBD-mNG localizes to the division site in early anaphase in pak1-ts rgf1+ cells at the restrictive temperature (35.5ºC, Fig. 7A, B). In agreement with our reasoning, early RBD-mNG localization in pak1-ts mutants at 35.5ºC was rescued in the absence of rgf1 (Fig. 10A, B).”

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Referee #3

Evidence, reproducibility and clarity

Onwubiko et al., present a clear and well written manuscript detailing the mechanistic understanding of how Rho1 is activated in a timely manner to ensure cytokinesis occurs in a scheduled manner at the end of telophase. Using fission yeast as a model system, and with the development of a novel Rho1 biosensor, they implicate a series of GTPases, exchange factors, GTPase activating proteins and kinases acting downstream of Cdc42 in the timely activation of Rho1. Specifically, they find that Cdc42 prevents premature Rho1 activation in early anaphase in a manner requiring the kinase Pak1. They observe that the Rho1 activators Rgf1 and Rgf3 localise to the division site in early anaphase, but Rho1 doesn't get activated until late anaphase, suggesting that control mechanisms ensure that these GEFs are held inactive, or that RhoGAP activity is able to balance this activation in early anaphase. This suppression of Rho1 activity in early anaphase requires Cdc42 and Pak1 and implicate (by omission) Rgf1, rather than Rgf3, is the relevant GEF.

I liked this manuscript, it was clearly written the experimental progression was logical and the data were easy to interpret from the figures. The conclusions were precise, believable and not overstated. The manuscript provides novel observations and through good use of a series of rescues/mutants, illuminates a pathway that is held in check by Cdc42 to ensure timely Rho1 activation. The novel Rho1 probe is exciting and shows well differently regulated pools of active Rho1 at the division site and the growing tips. I thought the co-imaging/measurement of ring placement and SBP duplication allowed a really clear understanding of the kinetics during this rapid phase of the cell cycle. A critique of the study is that the the mechanism by which Cdc42 controls Pak1, and by which Pak1 controls Rgf1/Rgf2 is left unclear. I guess there could always be a molecular expansion of these points (e.g., how does Cdc42 control Pak1; how does Pak1 control Rgf1; how is Rgf activity restricted when localised), but I think that would only enhance, rather than change, the level of detail of the paper's message. I think the paper's current conclusions stand on their own, the data is clear and believable, the experiments are well performed. There are a number of observations in the paper that are left open for future studies, and I think this is a positive (e.g., any separable role of Rgf1/Rgf2 and how Rga5 integrates into this pathway. As such, I am tempted to recommend accept with only minor amendments as outlined below.

1. P8 P15: should the call out be to Fig 2C, rather than 2B.
2. P14 L17: should it be 'gef1+ rgf3-', not 'gef1+, rgf3+'
3. Structure wise, I thought the section on Rga5 didn't really fit well on P16; it seemed sandwiched between two sections on GEFs. Is there a more appropriate place to place these data - perhaps between the paragraph breaks on P17? Related to this data, the conclusion on P16 suggests 'other' regulators of RhoGAP activity act to repress Rho1 function. Would 'additional' regulators of RhoGAP activity be more appropriate as there is some function contributed by Rga5?
4. In Fig 10b, you haven't defined orb2-34. Is it the rgf1-delete?
5. I find the sentence at the top of P18: 'Rho1 activation in pak1+ rgf1+....at 25oC and 35.5oc occurred at longer and similar SBP distances' quite hard to interpret. Could you perhaps expand it to make your message clearer?

Significance

I think the advance here is a genetic understanding of control mechanisms that order the exit from mitosis. The interplay between numerous GTPases and kinases must ensure a timely and ordered progression through M-exit, but it is often unclear how these activities are coordinated. A strength of the yeast system is that dependencies can be clearly visualised and the authors do a good job here to order the enzymatic activities needed to activate Rho1 in a timely manner for cytokinesis at the end of telophase.

I think this manuscript will be of interest to those interested in the cell biology of mitotic exit, the interplay between kinases and GTPases and those interested in the systems/netwoek biology of these processes. The description of a new Rho1 biosensor is an excellent tool for the community.

I am a cell biologist (mammalian) with interests in M-exit programmes that ensure a timely and ordered reestablishment of interphase architecture.

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Referee #2

Evidence, reproducibility and clarity

In many fungal cells, including fission yeast, the deposition of a new cell wall (a septum) between daughter cells is essential for cytokinesis. Cell wall synthases are trafficked to and activated at the division site, and dysregulated trafficking and/or synthase activation can lead to cytokinetic defects. In this study, the authors use fluorescent probes for Cdc42 and Rho1 activity and live-cell imaging to investigate the timing and regulation of Rho1 activity in fission yeast, and specifically, the role of Cdc42 in regulating Rho1. Summary of the proposed model: Gef1 -> active Cdc42 -> Pak1 --| Rgf1 -> active Rho1 -> septum formation

Major comments

1. As far as I can gather from the authors' description in the manuscript and quick literature search, this will be the first publication in S. pombe utilizing the HR1-C2 domain of Pkc2p as fluorescent probe for active Rho1 (RBD-mNG). While a comparable domain of S. cerevisiae Pkc1p (not "pck2" as referenced by the authors in Page 25) has been used for similar purposes, given the importance of this probe and the precedent it sets in the S. pombe literature, it is imperative that proper tests are performed to validate that its localization reflects activity of Rho1 and nothing else (such as membrane binding of the C2 domain or transcriptional regulation of the pkc2 promoter). Such tests should also be independent of the hypotheses central to the current study (i.e., effects of Gef1, Pak1, Rgf1/2 on the timing of RBD-mNG localization). Can the authors provide data to address this point? Examples include, but not limited to, rho1 mutants, expression of constitutively active Rho1, or temporary expression of dominant-negative Rho1.
2. Related, M&M does not provide sufficient details about the amino-acid positions corresponding to the "RBD" domain of Pkc2, thus precluding readers from reproducing the experiments. This needs to be clarified.
3. In Figure 1B, RBD1-mNG localizes clearly to the medial region of rho2∆ cells when the Rlc1-tdTomato ring has not formed. Does this mean that Rho2 has a major role in forming the contractile ring that is independent of Rho1 activation? On this other hand, however, data in Fig. S2BC suggest that RBD-mNG does not localize to the medial region in rho2∆ cells until Rlc1-tdTomato ring forms (the timing of which seems normal). This discrepancy needs to be addressed.
4. Given the nature of RBD-mNG localization, it seems unavoidable to have some level of arbitrariness in measuring the onset of its localization at the division site. It would be advisable for the authors to be specific in M&M about how they defined the onset of localization, i.e., whether it was based on universal threshold in signal intensity, ratio, etc. or on manual curation (ideally double-blind).

Minor comments

1. Throughout the manuscript, there are quite a few places where inconsistencies in genetic nomenclature can cause confusion to readers. Below are some examples. Figs. 6B, 7B, 10B: pak1(-ts), shk1, and orb2-34 (including faint labels under category marks in 6B). Fig. 9B (gef1+ rgf1∆) vs 9C (rgf1∆). Wild-type alleles are implicit in some figures, while explicit in others.
2. The first hypothesis (Fig. 1C) is that the AMR might regulate Rho1 activation. The ring is disrupted with LatA, but Rho remains active. They cite this as evidence that the AMR does not activate Rho1, but were the cells treated before or after the rings formed? If before, then the experiment demonstrates what the authors claim, but if after, it only shows that the AMR is not essential to maintain Rho activity.
3. Page 8: "Time-lapse imaging of cells simultaneously expressing CRIB-3xGFP and RBD-tdTomato [...] while Rho1 is activated ~20 minutes after SPB duplication (Fig. 2B)." This appears to refer to Fig. 2C.
4. Page 9: "[...] Rgf1 and Rgf3 localize as early as the time of ring assembly at an average SPB distance of 4-5 µm (Fig. 3D)." This sentence is confusing. How was the average calculated over the earliest ring assembly in non-time-lapse data? Fig. 3DE show distances between SPBs as short as 2.5 µm, not 4-5 µm, and average of ~8 µm for all cells at different stages of mitosis. This confusion needs to be clarified.
5. Fig. 5. Both the intensity and onset of RBD-mNG localization were affected by cdc42g12v expression. These two may form a causative relationship: reduced overall RBD signal may cause failed detection of early RBD localization. Can the authors compare cells with similar mean RBD-mNG signal intensities (Fig. 5B) and confirm that the timing of appearance at the division site is still delayed in gef1+ cdc42g12v relative to gef1+ empty?

Referees cross-commenting

I find all reviewer comments fair and have nothing specific to add.

Significance

The mechanisms governing septum formation during cytokinesis represent a key regulatory step in cytokinesis. Prior work showed that the Rho GTPases Cdc42 and Rho1 together control the timing of septum formation in S. pombe, and in S. cerevisiae, similar antagonistic regulation between Cdc42 and Rho1 has been reported previously (Atkins et al., J. Cell Biol. 2013 202: 231-240; Onishi et al., J Cell Biol. 2013 202: 311-329), but the precise molecular mechanisms remained unclear.

This is an important study that addresses the interplay between two major Rho-type small GTPases involved in cell division of many eukaryotic cells, and highlights their roles outside of the regulation of contractile ring. However, there are some issues that need to be addressed prior to publication, as listed above.

Keywords for the reviewer's field of expertise: S. pombe, S. cerevisiae, cytokinesis, Rho1, Cdc42, septum, MEN/SIN, genetics, cell biology, biochemistry.

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Referee #1

Evidence, reproducibility and clarity

This manuscript focuses on the role of Cdc42 in Rho1 activation during fission yeast cytokinesis. The primary finding is that active Cdc42 and its downstream effector Pak1 prevents accumulation of active Rho1 and the synthesis of cell wall material, at early stages of cytokinesis and despite the local recruitment of the Rho1 GEF Rgf1. The data supporting these conclusions are reasonably sound.

Additional experiments are presented to suggest that Cdc42 and Pak1 negatively regulate Rgf1, this conclusion is not as strongly supported (though it may be true)

These study relies on a newly described probe for active Rho1. However this probe is not sufficiently well validated.

Overall the manuscript was not assembled with sufficient care and rigor, these deficits could be readily corrected.

The major point of the paper is that Cdc42 and Pak1 negatively regulate Rho1 activation. However, during late cytokinesis, active Cdc42 and active Rho1 co-exist at the division site. Thus, Cdc42 activation induces a delay in Rho1 activation, but how this delay is overcome is not investigated or even discussed. Indeed, while the delay is shown the transience of this inhibition is not explicitly mentioned. At a minimum, the authors should highlight this point for the readers.

Specific points

1. • RBD probe This probe is central to this manuscript. However, there is insufficient validation of its target. Figure 1 shows the localization and its independence of Rho2. The authors should provide direct evidence that it recognizes Rho1 (for example using a repressible promotor or an anchor away approach).

At various places in the manuscript the authors refer to this probe as "Rho-probe", RBD-probe, RBD, RBD-(mNG or tdTomato). On page 11 the authors state, "As per our observations, we refer to the Rho-probe signal at the division site as active Rho1 from here onwards." Yet, in the very next paragraph they refer to the localization of the "Rho probe". This is also an issue with the figures. For example, in figures 4B,C ; 5B,C; 6B; 7B,C the figures are titled either "Rho1 activation at division site", "Rho1-probe at division site"; "Rho1-probe appearance at division site" ; "Rho1-probe in non-constricting rings". In fig 3, RBD-nNG is quantified in a graph entitled "localizaton [sic] of Rho1-GEFs at division site"

In all figures but two, 5c and 7c, the authors quantify Rho1 activation by the presence or absence of the probe, rather than a quantitative measure or the extent of recruitment of the probe. This could be analyzed my quantitatively. 2. - Regulation of Rgf1 by Cdc42 and Pak1. The results shown in figure 8 show that "early Rho1 activation in gef1 mutants is not Rgf3-dependent". Figure 9 establishes "loss of rgf1 prevents premature Rho1 activation in gef1Δ cells restoring it to normal in late anaphase (Fig.9A, B)." This finding indicates that Rgf1, but not Rgf3, is required for Rho1 premature activation. This finding doesn't rule out the possibility that Cdc42 and Pak1 might be required to turn off RhoGAPs to allow active Rho1 to accumulate. This analysis concludes with this unclear and ungrammatical sentence, "While we were unable to assess the Rho-probe in the rgf1Δ rgf2Δ double mutants due to its lethality [sic; is the Rho probe lethal?], our observations suggest that apart from Rgf1 early Rho1 activation in gef1Δ cells is either due to activation of Rgf2 or due to inhibition of Rga5." The conclusion that this regulation is due to control of Rgf1 should be toned down. E.g. from the abstract: "We provide functional and genetic evidence which indicates that Pak1 regulates Rho1 activation likely via the regulation of its GEF Rgf1."

Referees cross-commenting

I think reviews are appropriate and speak for themselves.

Significance

This manuscript ties together several recent papers from the author's lab on the control of Cdc42 activation during cytokinesis and older papers on the role of Rho1 in Bgs1 activation. It provides missing information into the temporal regulation of septum assembly.

The authors make a point of the similarities of fission yeast cytokinesis to animal cell cytokinesis. Indeed the second sentence reads, "The fission yeast model system divides via an actomyosin-based contractile ring, which is assembled in the medial region of the cell, as in animal cells (Balasubramanian et al., 2004; Pollard, 2010).". However, the authors fail to point out the many differences between yeast and animal cell cytokinesis until the last paragraph of the discussion. If the authors want to include the similarities in the introduction, they should also include the differences. For example, ring assembly is independent of Rho1 activation in fission yeast, but dependent on RhoA activation in animal cells.

This work will be of interest to biologists working on yeast cell division. To a lesser extent it will be of interest to biologists interested in cytokinesis and coordination of distinct GTPase pathways.

Additional points

1. • The text is overly wordy and needs extensive revision. Many of the experiments could be explained more clearly and with somewhat less genetic jargon. The introduction has quite a bit of extraneous information and lacks relevant facts, such as the function of Bgs1, which is central to the results.
2. • page 4 "GEFs promote GTP binding, thus keeping the GTPase active while the GAPs increase GTP hydrolysis, thus promoting GTPase inactivation." GEFs promote GTP binding, but they do not keep the GTPase active (an inhibitor of a RhoGAP would do that), they activate the GTPases.
3. • The current literature on animal cell cytokinesis indicates little direct role in cytokinesis, rather than the author's statement, "In larger eukaryotes, the role of Cdc42 activation has been reported mostly in meiotic division events such as polar body extrusion in oocytes, but not much is known about its role in cytokinesis in somatic cell division (Drechsel et al., 1997; Na and Zernicka-Goetz, 2006)." See for example, PMID 10898977, 10871280 which indicate Cdc42 does not play a major role during cytokinesis in at least a few systems where it has been analyzed.

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Reply to the reviewers

We thank the reviewers for their enthusiastic support for our work and their insightful comments and suggestions which we believe strengthen the manuscript. Below we detail how we propose to respond to each of the specific points raised by each reviewer.

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

• Summary:*

• In the article entitled "Unique functions of two overlapping PAX6 retinal enhancers", Uttley and coworkers characterize in detail the activity of two conserved human enhancers (i.e. NRE and HS5) previously reported to drive Pax6 expression to the neural retina. By integrating these enhancers in a PhiC31 landing site using a dual enhancer-reporter cassette, they generated a zebrafish stable line in which their activity can be followed by the expression of GFP (NRE) and mCherry (HS5). The authors show that although the enhancers have a partially overlapping activity at early stages (24hpf), later on (48 and 72hpf) they activity domains segregate: to stem cells and differentiated amacrine cells for NRE, and to proliferating progenitors and differentiated Müller glia cells for HS5. To this end they used two different approaches: a scRNA-seq analysis of sorted cells from the transgenic line and a immunofluorescent analysis employing cell specific markers. The authors conclude that their analysis allowed the identification of unique cell type-specific functions.*

• Major comments:*

• In general terms, the article is technically sound (please, see section B for an assessment of the significance of the findings). The methodology used and the data analysis are accurate. The work is well presented, the figures are clear, and the previous literature properly cited. My main concerns are the following:*

• 1) A general concern on the main conclusion of the work "the identification of unique cell type-specific functions for these enhancers". This is in my opinion only partially addressed by the study, as the conclusions are limited due to the absence of genetic experiments: such as deleting the enhancers in their native genomic context (either in human organoids or the homologous sequence in animal models), or at least assessing the effect of mutating their sequence in transgenesis assays in zebrafish. I understand that these functional assays may be out of the scope of the current work, but then the text should be toned down (the word "function" is extensively used) to make clear that the authors mean just expression. I would suggest substituting the word by "activity" in many instances.*

• The absence of further genetic experiments also limits the significance of the study (see section B).*

We appreciate and agree with the reviewer’s concern and would substitute the word “function” with “activity” throughout the manuscript.

2) Whereas the work in general is technically correct (particularly transgenic lines and scRNA-seq data are well described and presented), the co-expression analyses using cell-specific markers (figure 5) need to be improved. There are several issues here. First, the magnification shown is too low to appreciate the colocalization details in the figure. The panels should be replaced by others with higher magnification/resolution (see also minor comment on color-blind compatible images) * In addition, the selection of the markers is suboptimal. Although PCNA is a good general marker of the entire CMZ, it would be advisable to repeat the experiments using more specific markers of the stem cell niche (e.g. rx1, vsx2; Raymond et al 2006; BMC dev Biol) to better define the enhancers expression domain. In addition, HuC/D labels both RGCs and amacrines, and the colocalization could also be refined using amacrine specific markers (e.g. ptf1a : Jusuf & Harris 2009, Neural Dev).*

In the revised version of the manuscript, we would:

1. Provide higher magnification images as suggested by the reviewer

2. Provide additional stainings and justification for our choice of markers used in these colocalizaion experiments Minor comments:

3. 1.- The work includes several figures (1, 2, 5, 6 and S1) showing colocalization experiments in which channels are shown in red and green. I would advise replacing the red channel with magenta (or the green with cyan) in order to make the figures accessible to readers with color-blindness. This also applies to the schematic representations in figure 6.*

We will change the channel colours throughout the manuscript as suggested by the reviewers

2.- It is unclear in the text/images whether the expression driven by the HS5 enhancer is exclusively restricted to temporal retina throughout development (By the way, this differential nasal vs temporal expression should also be included in the final scheme in Figure 6). Does this mean that the expression of Pax6 in proliferating progenitors and Müller glia cells in the nasal retina is not controlled by this enhancer? To which extent is Pax6 needed to maintain the identity of these cell types?

We will modify the figures as suggested and also include more details of expression overlap with PAX6 expression in the text of the revised manuscript.

3.- The following sentence in the Discussion "To the best of our knowledge, ours is the first report where the activities of developmental enhancers have been mapped in vivo at single-cell resolution to reveal distinct patterns of activity" should be removed/rephrased. I would argue that the activity of cis-regulatory regions associated to any developmental gene are genome-wide mapped at single cell resolution in each scATACseq experiment.

We agree that scATAC-seq gives information about potentially active enhancers but it does not define the precise cell-types unless overlapped with expression data. Our method is aimed at ‘defining’ the precise cell-types where the enhancer is active and has the potential to be used to build high resolution maps of cell-type specific enhancer usage for loci with multiple enhancers driving a single gene. We will discuss this in detail in the revised version of the manuscript.

4.- In the methods section: * (a) FACS experiments: Please provide a supplementary Figure to graphically account for all gating/sorting strategies. * (b) ScRNA-seq analysis: Please provide the values of mean reads per cell and median genes per cell as obtained from Cell Ranger. This would be informative for others performing similar experiments

This will be included in the revised version of the manuscript.

**Referees cross-commenting** * I agree with the comments by reviewer #2 on the FACsorting experiments, the description of the landing sites, and the limited significance of the results.*

Reviewer #1 (Significance (Required)):

• As described in the previous section, the technical quality of this work is high in general terms. The experiments presented are clear and the conclusions straightforward. In that sense, the study will be a useful reference for those interested in the regulatory logic of Pax6 during eye development, including mainly developmental biologists and human geneticists. This may be particularly the case if new variants can be associated with these enhancers in microphthalmic patients.*

• The significance and novelty of the findings is however limited by several factors:*

• a) First, although the level of detail described in this article was not achieved previously, the human enhancers NRE and HS5 (or their conserved homologous in other vertebrates) were previously reported to drive Pax6 expression to the neural retina in transgenesis assays.(Kammandel et al 1999; Marquardt et al 2001; McBride et al 2011; Ravi et al 2013; Kim et al 2017).*

We agree that the enhancers we describe in this study have been studied before. However, we would like to argue that ours is the first study where we define precise cell-types for the activity of these enhancers. We will revise the discussion to strengthen this argument.

b) As mentioned in the previous section, the transgenesis assays are not complemented with genetic experiments. The function of the enhancers on retina differentiation and cell fate determination could have been investigated either by deleting them (or their homologous in different species) in their native context, or by exploring their regulatory grammar introducing point mutations or micro-deletions in transgenesis assays.

We agree that the suggested experiments would be useful for unambiguously establishing the functions of these enhancers and we will discuss these prospects in the revised version of the manuscript.

c) For reasons not explained in the text, the analysis focuses only in two of the many cis-regulatory regions controlling Pax6 expression in the retina (Lima Cunha et al 2019, Genes). In the absence of a more comprehensive analysis is difficult assessing the relevance of the findings here described.

We agree that other enhancers for the PAX6 locus should be investigated using similar analysis pipeline to build a complete picture of the enhancer mediated regulation of PAX6. We will discuss this in the revised version of the manuscript.

d) Finally, from a very general methodological point of view, the approach of using scRNA-seq to investigate enhance activity at a single-cell level is valid and original. However, it is unclear to which extent will be a useful method for many studies, particularly if the activity of endogenous elements is being assessed. In such cases, available scATAC-seq data will provide genome-wide information on the activity of any cis-regulatory element with cell resolution with no need for transgenesis assays and sorting experiments. * We thank the reviewer for recognising the novelty of the approach we describe in this manuscript. We will discuss the merits and demerits of our method with scATAC-seq experiments in the revised version of the manuscript.*

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

In this work, Uttley et al fine characterize two previously described Pax6 retinal enhancers (NRE and HS5) by combining QSTARZ transgénesis method in zebrafish (allowing to produce site-specific integrations of a dual enhancer reporter cassette), scRNAseq and co-immunostaining with specific markers for different retinal cell populations. * The work is experimentally very well performed and well presented and only minor considerations are raised below: * - Authors observe that a large fraction Of FACs sorted cells do not display expression of mCherry or EGFP RNAm in their scRNAseq analysis and attribute this to read dropout in the scRNAseq data and/ or to false-positive FAC cell selection. However, a third possibility exists: n fact due to the high stability of the EGFP and mCherry reporters cells or their progeny could maintain relatively high levels of these reporters even after transcriptional downregulation. Accordingly, the two reporters are strongly expressed in retinal precursor at early stages (24hpf). Thus, in my opinion, it is possible that some cells expressing these reporters retained significant EGFP/mCherry protein levels at 48hpf. Could the authors comment on this? Besides, authors could provide the FACsorting data to give an idea of whether only highly EGFP/ mCherry expressing cells were selected or whether also the low or mild expressing ones were included in the scRNAseq analysis. Finally, a combination of HCR/FSH and GFP//mCherry immunostaining could be used to assess whether a discrepancy in the protein vs mRNA distribution of the reporters exists. * - The authors could provide the information on the landing site used for the QSTARZ transgene integration. While from their previous publication (Bhatia et al 2021) I assume it is the chr6 landing site, it would be worth having this information in the manuscript, as well as a genotyping validation of the correct integration.*

We will address these points and provide relevant additional data where needed in the revised version of the manuscript.

**Referees cross-commenting** * I agree with all the points raised by reviewer 1. Particularly I also find that scATACseq experiments already allow testing, to some extent, enhancer activity at cellular level.*

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

• From the biological point of view the work provides only an incremental advance in our understanding of the functions of the HS5 and NRE PAX6 enhancers and of PAX6 regulation in the retina. In fact, unraveling the precise contribution of these enhancers to Pax6 retinal expression and the trans-regulatory code controlling their activity would require complex genetic experiments and would fall out of the scope of this work, requiring an extensive amount of work which could not be addressed in the short term. Thus, this work should be regarded as a methodological resource, with its main strength consisting of the use scRNAseq to fine-characterize enhancer activity.*

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Referee #2

Evidence, reproducibility and clarity

In this work, Uttley et al fine characterize two previously described Pax6 retinal enhancers (NRE and HS5) by combining QSTARZ transgénesis method in zebrafish (allowing to produce site-specific integrations of a dual enhancer reporter cassette), scRNAseq and co-immunostaining with specific markers for different retinal cell populations.

The work is experimentally very well performed and well presented and only minor considerations are raised below:

• Authors observe that a large fraction Of FACs sorted cells do not display expression of mCherry or EGFP RNAm in their scRNAseq analysis and attribute this to read dropout in the scRNAseq data and/ or to false-positive FAC cell selection. However, a third possibility exists: n fact due to the high stability of the EGFP and mCherry reporters cells or their progeny could maintain relatively high levels of these reporters even after transcriptional downregulation. Accordingly, the two reporters are strongly expressed in retinal precursor at early stages (24hpf). Thus, in my opinion, it is possible that some cells expressing these reporters retained significant EGFP/mCherry protein levels at 48hpf. Could the authors comment on this? Besides, authors could provide the FACsorting data to give an idea of whether only highly EGFP/ mCherry expressing cells were selected or whether also the low or mild expressing ones were included in the scRNAseq analysis. Finally, a combination of HCR/FSH and GFP//mCherry immunostaining could be used to assess whether a discrepancy in the protein vs mRNA distribution of the reporters exists.
• The authors could provide the information on the landing site used for the QSTARZ transgene integration. While from their previous publication (Bhatia et al 2021) I assume it is the chr6 landing site, it would be worth having this information in the manuscript, as well as a genotyping validation of the correct integration.

Referees cross-commenting I agree with all the points raised by reviewer 1. Particularly I also find that scATACseq experiments already allow testing, to some extent, enhancer activity at cellular level.

Significance

From the biological point of view the work provides only an incremental advance in our understanding of the functions of the HS5 and NRE PAX6 enhancers and of PAX6 regulation in the retina. In fact, unraveling the precise contribution of these enhancers to Pax6 retinal expression and the trans-regulatory code controlling their activity would require complex genetic experiments and would fall out of the scope of this work, requiring an extensive amount of work which could not be addressed in the short term. Thus, this work should be regarded as a methodological resource, with its main strength consisting of the use scRNAseq to fine-characterize enhancer activity.

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 the article entitled "Unique functions of two overlapping PAX6 retinal enhancers", Uttley and coworkers characterize in detail the activity of two conserved human enhancers (i.e. NRE and HS5) previously reported to drive Pax6 expression to the neural retina. By integrating these enhancers in a PhiC31 landing site using a dual enhancer-reporter cassette, they generated a zebrafish stable line in which their activity can be followed by the expression of GFP (NRE) and mCherry (HS5). The authors show that although the enhancers have a partially overlapping activity at early stages (24hpf), later on (48 and 72hpf) they activity domains segregate: to stem cells and differentiated amacrine cells for NRE, and to proliferating progenitors and differentiated Müller glia cells for HS5. To this end they used two different approaches: a scRNA-seq analysis of sorted cells from the transgenic line and a immunofluorescent analysis employing cell specific markers. The authors conclude that their analysis allowed the identification of unique cell type-specific functions.

Major comments:

In general terms, the article is technically sound (please, see section B for an assessment of the significance of the findings). The methodology used and the data analysis are accurate. The work is well presented, the figures are clear, and the previous literature properly cited. My main concerns are the following:

1. A general concern on the main conclusion of the work "the identification of unique cell type-specific functions for these enhancers". This is in my opinion only partially addressed by the study, as the conclusions are limited due to the absence of genetic experiments: such as deleting the enhancers in their native genomic context (either in human organoids or the homologous sequence in animal models), or at least assessing the effect of mutating their sequence in transgenesis assays in zebrafish. I understand that these functional assays may be out of the scope of the current work, but then the text should be toned down (the word "function" is extensively used) to make clear that the authors mean just expression. I would suggest substituting the word by "activity" in many instances. The absence of further genetic experiments also limits the significance of the study (see section B).
2. Whereas the work in general is technically correct (particularly transgenic lines and scRNA-seq data are well described and presented), the co-expression analyses using cell-specific markers (figure 5) need to be improved. There are several issues here. First, the magnification shown is too low to appreciate the colocalization details in the figure. The panels should be replaced by others with higher magnification/resolution (see also minor comment on color-blind compatible images) In addition, the selection of the markers is suboptimal. Although PCNA is a good general marker of the entire CMZ, it would be advisable to repeat the experiments using more specific markers of the stem cell niche (e.g. rx1, vsx2; Raymond et al 2006; BMC dev Biol) to better define the enhancers expression domain. In addition, HuC/D labels both RGCs and amacrines, and the colocalization could also be refined using amacrine specific markers (e.g. ptf1a : Jusuf & Harris 2009, Neural Dev).

Minor comments:

1. The work includes several figures (1, 2, 5, 6 and S1) showing colocalization experiments in which channels are shown in red and green. I would advise replacing the red channel with magenta (or the green with cyan) in order to make the figures accessible to readers with color-blindness. This also applies to the schematic representations in figure 6.
2. It is unclear in the text/images whether the expression driven by the HS5 enhancer is exclusively restricted to temporal retina throughout development (By the way, this differential nasal vs temporal expression should also be included in the final scheme in Figure 6). Does this mean that the expression of Pax6 in proliferating progenitors and Müller glia cells in the nasal retina is not controlled by this enhancer? To which extent is Pax6 needed to maintain the identity of these cell types?
3. The following sentence in the Discussion "To the best of our knowledge, ours is the first report where the activities of developmental enhancers have been mapped in vivo at single-cell resolution to reveal distinct patterns of activity" should be removed/rephrased. I would argue that the activity of cis-regulatory regions associated to any developmental gene are genome-wide mapped at single cell resolution in each scATACseq experiment.
4. In the methods section:
   • (a) FACS experiments: Please provide a supplementary Figure to graphically account for all gating/sorting strategies.
   • (b) ScRNA-seq analysis: Please provide the values of mean reads per cell and median genes per cell as obtained from Cell Ranger. This would be informative for others performing similar experiments

Referees cross-commenting I agree with the comments by reviewer #2 on the FACsorting experiments, the description of the landing sites, and the limited significance of the results.

Significance

As described in the previous section, the technical quality of this work is high in general terms. The experiments presented are clear and the conclusions straightforward. In that sense, the study will be a useful reference for those interested in the regulatory logic of Pax6 during eye development, including mainly developmental biologists and human geneticists. This may be particularly the case if new variants can be associated with these enhancers in microphthalmic patients.

The significance and novelty of the findings is however limited by several factors:

• a) First, although the level of detail described in this article was not achieved previously, the human enhancers NRE and HS5 (or their conserved homologous in other vertebrates) were previously reported to drive Pax6 expression to the neural retina in transgenesis assays.(Kammandel et al 1999; Marquardt et al 2001; McBride et al 2011; Ravi et al 2013; Kim et al 2017).
• b) As mentioned in the previous section, the transgenesis assays are not complemented with genetic experiments. The function of the enhancers on retina differentiation and cell fate determination could have been investigated either by deleting them (or their homologous in different species) in their native context, or by exploring their regulatory grammar introducing point mutations or micro-deletions in transgenesis assays.
• c) For reasons not explained in the text, the analysis focuses only in two of the many cis-regulatory regions controlling Pax6 expression in the retina (Lima Cunha et al 2019, Genes). In the absence of a more comprehensive analysis is difficult assessing the relevance of the findings here described.
• d) Finally, from a very general methodological point of view, the approach of using scRNA-seq to investigate enhance activity at a single-cell level is valid and original. However, it is unclear to which extent will be a useful method for many studies, particularly if the activity of endogenous elements is being assessed. In such cases, available scATAC-seq data will provide genome-wide information on the activity of any cis-regulatory element with cell resolution with no need for transgenesis assays and sorting experiments.