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Reply to the reviewers

Note : The original preprint version of our manuscript has been reviewed by 3 subject experts for Review Commons. All the three reviewers’ comments on the original version of our manuscript have been fully addressed. Their input was extremely valuable in helping us clarify and refine the presentation of our results and conclusions. Their feedback contributed to making the study both more thoroughly developed and more accessible to a broad readership, while preserving its mechanistic depth. We believe that this revised version more effectively highlights the conceptual advances brought by our findings.

Reviewer #1

Evidence, reproducibility and clarity

The manuscript "Key roles of the zona pellucida and perivitelline space in promoting gamete fusion and fast block to polyspermy inferred from the choreography of spermatozoa in mice oocytes" by Dr. Gourier and colleagues explores the poorly understood process of gamete fusion and the subsequent block to polyspermy by live-cell imaging of mouse oocytes with intact zona pellucida in vitro. The new component in this study is the presence of the ZP, which in prior studies of live-cell imaging had been removed before. This allowed the authos to examine contributions of the ZP to the block in polyspermy in relation to the timing of sperm penetrating the ZP and sperm fusing with the oocyte. By carefully analysing the timing of the cascade of events, the authors find that the first sperm that reaches the membrane of the mouse oocyte is not necessarily the one that fertilizes the oocytes, revealing that other mechanisms post-ZP-penetration influence the success of individual sperm. While the rate of ZP penetration remains constant in unfertilized oocytes, it decreases upon fertilization for subsequent sperm, providing direct evidence for the known 'slow block to polyspermy' provided by changes to the ZP adhesion/ability to be penetrated. Careful statistical analyses allow the authors to revisit the role of the ZP in preventing polyspermy: They show that the ZP block resulting from the cortical reaction is too slow (in the range of an hour) to contribute to the immediate prevention of polyspermy in mice. The presented analyses reveal that the ZP does contribute to the block to polyspermy in two other ways, namely by effectively limiting the number of sperm that reach the oocyte surface in a fertilization-independent manner, and by retaining components like JUNO and CD9, that are shed from the oocyte plasma membrane after fertilization, in the perivitelline space, which may help neutralize surplus spermatozoa that are already present in the PVS. Lastly, the authors report that the ZP may also contribute to channeling the flagellar oscillations of spermatozoa in the PVS to promote their fusion competence.

Major comments:

• Are the key conclusions convincing?

The authors provide a careful analysis of the dynamics of events, though the analyses are correlative, and can only be suggestive of causation. While this is a limitation of the study, it provides important analysis for future research. Moreover, by analysing also control oocytes without fertilization and the timing of events, the authors have in some instances clear 'negative controls' for comparison.

Some claims would benefit from rewording or rephrasing to put the findings better in the context of what is already known and what is novel:

• the phrasing 'challenging prior dogma' might be too strong since it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg (though I am afraid that I do not have any citations or references for this). However, given that in the field people generally think it is not necessarily and always the first sperm, the authors may want to consider weakening this claim.

Only real-time imaging of in vitro fertilization of zona pellucida-intact oocytes, as performed in our study, is capable of determining which spermatozoon crossing the zona pellucida fuses with the oocyte. However, such studies are rare, and most do not specifically address this question. As Reviewers 1 & 3, we have not found any citation or reference telling or showing that it is not necessarily the first spermatozoon to penetrate the zona pellucida that fertilizes the egg. In contrast, at least one reference (Sato et al., 1979) explicitly reports the opposite. If, as suggested by Reviewer 1 and 3, it has indeed been observed before that the first sperm to pass the ZP is not always the one that fertilizes, and if this idea is generally accepted in the field, then it is all the more important that a study demonstrates and publishes this point. This is precisely what our study makes possible. However, in case we may have overlooked a previous reference making the same observation as ours, we have removed the phrasing ‘challenging prior dogma’. That being said, the key issue is not so much that it is not necessarily the first spermatozoon penetrating the perivitelline space that fertilizes, but rather why spermatozoa that successfully reach the PVS of an unfertilized oocyte may fail to achieve fertilization. This is one of the central questions our study sought to address.

• I do think the cortical granule release could still contribute to the block to polyspermy though - as the authors here nicely show - at a later time-point only, and thus not the major and not the immediate block as previously thought. The wording in the abstract should therefore be adjusted (since it could still contribute...)

We are concerned that we may disagree on this point. The penetration block resulting from cortical granule release progressively reduces the permeability of the zona pellucida to spermatozoa, relative to its baseline permeability prior to sperm–oocyte fusion. Any decrease in this baseline permeability occurring before the fusion block becomes fully effective can contribute to the prevention of polyspermy by limiting the number of sperm that can access the oolemma at a time when fusion is still possible. In contrast, once the fusion block is fully established, limiting the number of spermatozoa traversing the ZP becomes irrelevant regarding the block to polyspermy, as the fusion block alone is sufficient to prevent additional fertilizations, rendering the penetration block obsolete. The only scenario that could challenge this obsolescence is if the fusion block were transient. In that case, as Reviewer 1 suggests, the penetration block could indeed play a role at a later time-point. However, taken together, our study and that of Nozawa et al. (2018) support the conclusion that this is not the case in mice:

• Our in vitro study using kinetic tracking shows that the time constant for completion of the fusion block is typically 6.2 ± 1.3 minutes. During this time window, we observe that the permeability of the zona pellucida to spermatozoa does not yet decrease significantly from the baseline level it exhibited prior to sperm–oocyte fusion (see Figures 5B and S1B in the revised manuscript, and Figures 5A and 5B in the initial version). Consequently, before the fusion block is fully established, the penetration block can contribute only marginally—if at all—to the prevention of polyspermy. In contrast, the naturally low baseline permeability of the ZP—independent of any fertilization-triggered penetration block—as well as the relatively long timing of fusion ( minutes on average) after sperm penetration in the perivitelline space, are factors that contribute to the preservation of monospermic while the fusion block is still being established.
• Our in vitro study using kinetic tracking shows that once the fusion block is completed following the first fusion event, no additional spermatozoa are able to fuse with the oocyte until the end of the experiment, 4 hours post-insemination (see blue points and fitting curve in Figure 5C). Meanwhile, one or more additional spermatozoa—most of them motile and therefore viable—are present in the perivitelline space in 50% of the oocytes analyzed (purple point in Figure 5C). This demonstrates that, once established, the fusion block remains effective for at least the entire duration of the experiment, supporting the idea of a fully functional and long-lasting fusion block.
• Nozawa et al. (2018) found that female mice lacking ovastacin—the protease released during the cortical reaction that renders the zona pellucida impenetrable—are normally fertile. They additionally reported that the oocytes recovered from these females after mating are monospermic despite the systematic presence of additional spermatozoa in the perivitelline space. These findings further support the conclusion that in mice the fusion block is both permanent and sufficient to prevent polyspermy. For all these reasons, we believe that even at a later time-point, the penetration block does not contribute to the prevention of polyspermy in mice.

To clarify the fact that the penetration block does not necessarily contribute to prevent polyspermy, which indeed challenges the commonly accepted view, we have substantially revised the discussion. Furthermore, Figure 9 from the initial version of the manuscript has been replaced by Figure 8 in the revised version. This new figure provides a more didactic illustration of the inefficacy of the penetration block in preventing polyspermy in mice, by showing the respective impact of the fusion block, the penetration block, as well as fusion timing and the natural baseline permeability of the zona pellucida, on the occurrence of polyspermy.

As for the abstract, it has also been thoroughly revised. The content related to this section is now expressed in a way that emphasizes the factors that actively contribute to the prevention of polyspermy in mice, rather than those with no or marginal contribution (such as the penetration block in this case).

• release of OPM components - in the abstract it's unclear what the authors mean by this - in the results part it becomes clear. Please already make it clear in the abstract that it is the fertility factors JUNO/CD9 that could bind to sperm heads upon their release and thus 'neutralize' them? I would also recommend not referring to it as 'outer' plasma membrane (there is no 'inner plasma membrane'). Moreover, in the abstract please clarify that this release is happening only after fusion of the first sperm and not all the time. In the abstract it sounds as if this was a completely new idea, but there is good prior evidence that this is in fact happening (as also then cited in the results part) - maybe frame it more as the retention inside the PVS as new finding.

We thank reviewer 1 for pointing out the lack of precision in the abstract regarding the “components” released from the oolemma, and the fact that our phrasing may have given the impression that the post-fertilization release of CD9 and JUNO is a novel observation. The new observation is that CD9 and JUNO, which are known to be massively released from the oolemma after fertilization, bind to spermatozoa in the perivitelline space. However, we cannot rule out the possibility that other oocyte-derived molecules not investigated here may undergo a similar process. This is why we employed the broader term “components”, which encompasses both CD9 and JUNO as well as potential additional molecules. That said, we acknowledge the lack of precision introduced by this terminology. To address this, we have revised the corresponding sentence in the abstract to better reflect our new findings relative to previous ones, and to eliminate the ambiguity introduced by the word “component”.

The revised sentence of the abstract reads as follows:

“Our observation that non-fertilizing spermatozoa in the perivitelline space are coated with CD9 and JUNO oocyte’s proteins, which are known to be massively released from the oolemma after gamete fusion, supports the hypothesis that the fusion block involves an effective perivitelline space-block contribution consisting in the neutralization of supernumerary spermatozoa in the perivitelline space by these and potentially other oocyte-derived factors.”

Moreover, we cannot state in the abstract that the release of CD9 and JUNO occurs only after the fusion of the first spermatozoon and not before, since some CD9 and JUNO are already detectable in the perivitelline space (PVS) prior to fusion. What our study shows is that, before fertilization, CD9 and JUNO are predominantly localized at the oocyte membrane. In contrast, after fusion (four hours post-insemination), oocyte CD9 is distributed between the membrane and the PVS, and the only JUNO signal detectable in the oocyte is found in the PVS. This is what we describe in the Results section on page 15.

Regarding the acronym “OPM” in the initial version of the manuscript, although it was defined in the introduction as referring to the oocyte plasma membrane and not the outer plasma membrane (which, indeed, would not be meaningful), we acknowledge that it may have caused confusion to people in the field due to its resemblance to the commonly used meaningful acronym “OAM” for outer acrosomal membrane. To avoid any ambiguity, we have replaced the acronym “OPM” throughout the revised manuscript with the term “oolemma”, which unambiguously refers to the plasma membrane of the oocyte.

It is unclear to me what the relevance of dividing the post-fusion/post-engulfment into different phases as done in Fig 2 (phase 1, and phase 2) - also for the conclusions of this paper this seems rather irrelevant and overly complicated, since the authors never get back to it and don't need it (it's not related to the polyspermy block analyses). I would remove it from the main figures and not divide into those phases since it is distracting from the main focus.

Sperm engulfment and PB2 extrusion are two processes that follow sperm–oocyte fusion. As such, they are clear indicators that fusion has occurred and that meiosis has resumed. Their progression over time is readily identifiable in bright-field imaging: sperm engulfment is characterized by the gradual disappearance of the spermatozoon head from the oolemma, whereas PB2 extrusion is observed as the progressive emergence of a rounded protrusion from the oocyte membrane (Figure 2 in the initial manuscript and Figure S2 A&B in the revised version). The kinetics of these events, measured from the arrest of “push-up–like” movement of the sperm head against the oolemma —assumed to coincide with sperm-oocyte fusion, as further justified in a later response to Reviewer 1—provide reliable temporal landmarks for estimating the timing of fusion when the fusion event itself is not directly observed in real time (Figure S2 C&D).

The four landmarks used in this estimation are:

(i) the disappearance of the sperm head from the oolemma due to internalization (28 ± 2 minutes post-arrest, mean ± SD);

(ii) the onset of PB2 protrusion from the oolemma (28 ± 2 minutes post-arrest);

(iii) the moment when the contact angle between the PB2 protrusion and the oolemma shifts from greater than to less than 90° (49 ± 6 minutes post-arrest);

(iv) the completion of PB2 extrusion (73 ± 10 minutes post-arrest).

The approach used to determine the fusion time window of a fertilizing spermatozoon from these landmarks is detailed in the “Determination of the Fertilization Time Windows” section of the Materials and Methods. Compared to the initial version of the manuscript, we have added a paragraph explaining the rationale for using the arrest of the push-up–like movement as a reliable indicator for sperm–oocyte fusion and have clarified the description of the approach used to determine fertilization timing.

The timed characterization of sperm engulfment and PB2 extrusion kinetics is highly relevant to the analysis of the penetration and fusion blocks, however we agree that its place is more appropriate in the Supplementary Information than in the main text. In accordance with the reviewer’s recommendation, this section has therefore been moved to the Supplementary Information SI2.

For the statistical analysis, I am not sure whether the assumption "assumption that the probability distribution of penetration or fertilization is uniform within a given time window" is in fact true since the probability of fertilizing decreases after the first fertilization event.... Maybe I misunderstood this, but this needs to be explained (or clarified) better, or the limitation of this assumption needs to be highlighted.

During in vitro fertilization experiments with kinetic tracking, each oocyte is observed sequentially in turn. As a result, sperm penetration into the perivitelline space or fusion with the oolemma may occur either during an observation round or in the interval between two rounds. In the former case, penetration or fusion is directly observed in real time, allowing for high temporal precision in determining the moment of the event. In contrast, when penetration or fusion occurs between two observation rounds, the precise timing cannot be directly determined. We can only ascertain that the event took place within the time window we have determined. Because, within a given penetration or fusion time window, we do not know the exact moment at which the event occurred, there is no reason to favor one time over another. This justifies the assumption that all time points within the window are equally probable. This explanation has been added in the section Statistical treatment of penetration and fertilization chronograms to study the kinetics of fertilization, penetration block and fusion block of the main text and in the section Statistical treatment of penetrations and fertilizations chronograms to study penetration and fusion blocks of the material and methods.

-Suggestion for additional experiments:

If I understood correctly, the onset of fusion in Fig 2C is defined by stopping of sperm beating? If it is by the sudden stop of the beating flagellum, this should be confirmed in this situation (with the ZP intact) that it correctly defines the time-point of fusion since this has not been measured in this set-up before as far as I understand. In order to measure this accurately, the authors will need to measure this accurate to be able to acquire those numbers (of time from fusion to end of engulfment), e.g. by pre-loading the oocyte with Hoechst to transfer Hoechst to the fusing sperm upon membrane fusion.

The nuclear dye Hoechst is widely used as a marker of gamete fusion, as it transfers from the ooplasm—when preloaded with the dye—into the sperm nucleus upon membrane fusion, thereby signaling the happening of the fusion event. This technique is applicable in the context of in vitro fertilization using ZP-free oocytes. However, it is not suitable when cumulus–oocyte complexes are inseminated, as is the case in both in vitro experimental conditions of the present study (standard IVF and IVF with kinetic tracking). Indeed, when cumulus–oocyte complexes are incubated with Hoechst to preload the oocytes, the numerous surrounding cumulus cells also take up the dye. Consequently, upon insemination, spermatozoa acquire fluorescence while traversing and dispersing the cumulus mass—before reaching the ZP—thus rendering Hoechst labeling ineffective as a specific marker of membrane fusion. This remains true even under optimized conditions involving brief Hoechst incubation of cumulus–oocyte complexes ( Nonetheless, we have strong evidence supporting the use of the arrest of sperm movement as a surrogate marker for the moment of fusion. In our previous study (Ravaux et al., 2016; ref. 4 in the revised manuscript), we investigated the temporal relationship between the abrupt cessation of sperm head movement on the oolemma—resulting from strong flagellar beating arrest—and the fusion event, using ZP-free oocytes preloaded with Hoechst. That study revealed a temporal delay of less than one minute between the cessation of sperm oscillations and the actual membrane fusion, thereby supporting the conclusion that in ZP-free oocytes, the arrest of vigorous sperm movement at the oolemma is a reliable indicator of the moment at which fusion occurs. In the same study, the kinetics of sperm head internalization into the ooplasm were also characterized, typically concluding within 20–30 minutes after movement cessation. These findings are fully consistent with our current observations in ZP-intact oocytes, where sperm head engulfment was completed approximately 24 ± 3 minutes after the arrest of sperm oscillations. Taken together, these results strongly support the conclusion that, in both ZP-free and ZP-intact oocytes, the arrest of sperm movement is a reliable indicator of the fusion event. This assumption formed the basis for our determination of fertilization time points in the present study.

These justifications were not fully detailed in the original version of the manuscript. We have addressed this in the revised version by explicitly presenting this rationale in the Materials and Methods section under Determination of the Fertilization Time Windows.

Fig 8: 2 comments

• To better show JUNO/CD9 pre-fusion attachment to the oocyte surface and post-fusion loss from the oocyte surface (but persistence in the PVS), an image after removal of the ZP (both for pre-fertilization and post-fertilization) would be helpful - the combination of those images with the ones you have (ZP intact) would make your point more visible.

We have followed this recommendation. Figure 8 of the initial manuscript has been replaced by Figure 6 in the revised manuscript, which illustrates the four situations encountered in this study: fertilized and unfertilized oocytes, each with and without unfused spermatozoa in their PVS. To better show JUNO/CD9 pre-fusion presence to the oocyte plasma membrane, as well as their post-fusion partial (for CD9) and near-complete (for JUNO) loss from the oocyte membrane (but persistence in the PVS), paired images of the same oocyte before and after of ZP removal are now provided, both for unfertilized (Figure 6A) and fertilized oocytes (Figure 6C).

• You show that the heads of spermatozoa post fusion are covered in CD9 and JUNO, yet I was missing an image of sperm in the PVS pre-fertilization (which should then not yet be covered).

As staining and confocal imaging of the oocytes were performed 4 hours after insemination, images of sperm in the PVS of an oocyte “pre-fertilization” cannot be strictly obtained. However, we can have images of spermatozoa present in the PVS of oocytes that remained unfertilized. This situation, now illustrated in Figure 6B of the revised manuscript, shows that these spermatozoa are also covered in JUNO and CD9, which they may have progressively acquired over time from the baseline presence of these proteins in the PVS of unfertilized oocytes. This also may provide a mechanistic explanation for their inability to fuse with the oolemma, and, consequently, for the failure of fertilization in these oocytes.

Minor comments:

• The videos were remarkable to look at, and great to view in full. However, for the sake of time, the authors might want to consider cropping them for the individual phases to have a shorter video (with clear crop indicators) with the most important different stages visible in a for example 1 min video (e.g. video.

We have followed this recommendation. The videos have been cropped and annotated in order to highlight the key events that support the points made in the result section from page 9 to 11 in the revised manuscript.

• In general, given that the ZP, PVS and oocyte membrane are important components, a general scheme at the very beginning outlining the relative positioning of each before and during fertilization (and then possibly also including the second polar body release) would be extremely helpful for the reader to orient themselves.

A general scheme addressing Reviewer 1 request, summarizing the key components and concepts discussed in the article and intended to help guide the reader, has been added to the introduction of the revised manuscript as Figure 1.

• first header results "Multi-penetration and polyspermy under in vivo conditions and standard and kinetics in vitro fertilization conditions" is hard to understand - simplify/make clearer (comparison of in vivo and in vitro conditions? Establishing the in vitro condition as assay?)

The title of the first Results section has been revised in accordance with Reviewer 1 suggestion. It now reads: Comparative study of penetration and fertilization rates under in vivo and two distinct in vitro fertilization conditions.

• Large parts of the statistical analysis (the more technical parts) could be moved to the methods part since it disrupts the flow of the text.

In the revised version of our manuscript, we have restructured this part of the analysis to ensure that more technical or secondary elements do not disrupt the flow of the main text. Accordingly, the equations have been reduced to only what is strictly necessary to understand our approach, their notation has been greatly simplified, and the statistical analysis of unfertilized oocytes whose zona pellucida was traversed by one or more spermatozoa has been moved to the Supplementary Information (SI1).

• To me, one of the main conclusions was given in the text of the results part, namely that "This suggests that first fertilization contributes effectively to the fertilization-block, but less so to the penetration block". I would suggest that the authors use this conclusion to strengthen their rationale and storyline in the abstract.

We agree with Reviewer 1 suggestion. Accordingly, we have not only thoroughly revised our abstract, but also the introduction and discussion, in order to better highlight the rationale of our study, its storyline, and the new findings which not only challenge certain established views but also open new research directions in the mechanisms of gamete fusion and polyspermy prevention.

• Wording: To characterize the kinetics with which penetration of spermatozoa in the PVS falls down after a first fertilization," falls down should be replaced with decreases (page 10 and page 12)

Falls down has been removed from the new version and replaced with decreases

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Significance

Overall, this manuscript provides very interesting and carefully obtained data which provides important new insights particularly for reproductive biology. I applaud the authors on first establishing the in vivo conditions (how often do multiple sperm even penetrate the ZP in vivo) since studies have usually just started with in vitro condition where sperm at much higher concentration is added to isolated oocyte complexes. Thank you for providing an in vivo benchmark for the frequency of multiple sperm being in the PVS. While this frequency is rather low (somewhat expectedly, with 16% showing 2-3 sperm in the PVS), this condition clearly exists, providing a clear rationale for the investigation of mechanisms that can prevent additional sperm from entering.

My own expertise is experimentally - thus I don't have sufficient expertise to evaluate the statistical methods employed here.

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Reviewer #2

Evidence, reproducibility and clarity

Overall, this is a very interesting and relevant work for the field of fertilization. In general, the experimental strategies are adequate and well carried out. I have some questions and suggestions that should be considered before the work is published.

1) Why are the cumulus cells not mentioned when the AR is triggered before or while the sperms cross it? It seems the paper assumes from previous work that all sperm that reach ZP and the OPM have carried out the acrosome reaction. This, though probably correct, is still a matter of controversy and should be discussed. It is in a way strange that the authors do not make some controls using sperm from mice expressing GFP in the acrosome, as they have used in their previous work.

We do not mention the cumulus cells or whether the acrosome reaction is triggered before, during, or after their traversal (i.e., upon sperm binding to the ZP), as this question, while scientifically relevant, pertains to a distinct line of investigation that lies beyond the scope of the present study. Even with the use of spermatozoa expressing GFP in the acrosome, addressing this question would require a complete redesign of our kinetic tracking protocol, which was specifically conceived to monitor in bright field the dynamic behavior of spermatozoa from the moment they begin to penetrate the perivitelline space of an oocyte. Accordingly, we imaged oocytes that were isolated 15 minutes after insemination of the cumulus–oocyte complexes, by which time most (if not all) cumulus cells had detached from the oocytes, as explained in the fourth paragraph of the material and methods of both the initial and revised versions of the manuscript. The spermatozoa we had access to were therefore already bound to the zona pellucida at the time of removal from the insemination medium, and had thus necessarily passed through the cumulus layer. It is unclear for us why Reviewer 2 believes that we “assume from previous work that all sperm that reach ZP has carried out the acrosome reaction”. We could not find any statement in our manuscript suggesting, let alone asserting, such an assumption, which we know to be incorrect. Based on both published work from Hirohashi’s group in 2011 (Jin et al., 2011, DOI: 10.1073/pnas.1018202108) and our own unpublished observation (both involving cumulus-oocyte masses inseminated with spermatozoa expressing GFP in the acrosome), it is established that only a subset of spermatozoa reaching the ZP after crossing the cumulus layer has undergone acrosome reaction. Moreover, from the same sources—as well as from a recent publication by Buffone’s group (Jabloñsky et al., 2023 DOI: 10.7554/eLife.93792 ) which is the one to which reviewer 2 refers in her/his 3rd comment, it is also well established that spermatozoa have all undergone acrosome reaction when they enter the PVS. To the best of our knowledge, this latter point has long been widely accepted and is not questioned. Therefore, stating this in the first paragraph of the Discussion in the revised manuscript, while referencing the two aforementioned published studies, should be appropriate. What remains a matter of ongoing debate, however, is the timing and the physiological trigger(s) of the acrosome reaction in fertilizing spermatozoa. The 2011 study by Hirohashi’s group challenged the previously accepted view that ZP binding induces the acrosome reaction, showing instead that most spermatozoa capable of crossing the ZP and fertilizing the oocyte had already undergone the acrosome reaction prior to ZP binding. However, as this issue lies beyond the scope of our study, we do not consider it appropriate to include a discussion of it in the manuscript.

2) In the penetration block equations, it is not clear to me why (𝑡𝑃𝐹1) refers to both PIPF1 and 𝜎𝜎𝑃I𝑃𝐹1. Is it as function off?

That is correct: (tPF1) means function of the time post-first fertilization. Both the post-first fertilization penetration index (i.e. PIPF1) and its incertainty (i.e. 𝜎𝑃I𝑃𝐹1 ) vary as a function of this time. However, as mentioned in a previous response to Reviewer 1, this section has been rewritten to improve clarity and readability. The equations have been limited to those strictly necessary for understanding our approach, and their notation has been significantly simplified.

3) Why do the authors think that the flagella stops. The submission date was 2024-10-01 07:27:26 and there has been a paper in biorxiv for a while that merits mention and discussion in this work (bioRxiv [Preprint]. 2024 Jul 2:2023.06.22.546073. doi: 10.1101/2023.06.22.546073.PMID: 37904966).

Our experimental approach allows us to determine when the spermatozoon stops moving, but not why it stops. We thank Reviewer 3 for pointing out this very relevant paper from Buffone’s group (doi: 10.7554/eLife.93792) which shows the existence of two distinct populations of live, acrosome-reacted spermatozoa. These correspond to two successive stages, which occur either immediately upon acrosome reaction in a subset of spermatozoa, or after a variable delay in others, during which the sperm transitions from a motile to an immotile state. The transition from the first to the second stage was shown to follow a defined sequence: an increase in the sperm calcium concentration, followed by midpiece contraction associated with a local reorganization of the helical actin cortex, and ultimately the arrest of sperm motility. For fertilizing spermatozoa in the PVS, this transition was shown to occur upon fusion. However, it was also reported in some non-fertilizing spermatozoa that this transition took place within the PVS. These findings are consistent with the requirement for sperm motility in order to achieve fusion with the oolemma. Moreover, the fact that some spermatozoa may prematurely transition to the immotile state within the PVS can therefore be added to the list of possible reasons why a spermatozoon that penetrates the PVS of an oocyte might fail to fuse.

This discussion has been added to the first paragraph of the Discussion section of our revised manuscript.

4) Please correct at the beginning of Materials and Methos: Sperm was obtained from WT male mice, it should say were.

Thank you, the correction has been done.

5) This is also the case in the fourth paragraph of this section: oocyte were not was.

The sentence in question has been modified as followed: “In the in vitro fertilization experiments with kinetic tracking, a subset of oocytes—together with their associated ZP-bound spermatozoa—was isolated 15 minutes post-insemination and transferred individually into microdrops of fertilization medium to enable identification.”

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Significance

Understanding mammalian gamete fusion and polyspermy inhibition has not been fully achieved. The authors examined real time brightfield and confocal images of inseminated ZP-intact mouse oocytes and used statistical analyses to accurately determine the dynamics of the events that lead to fusion and involve polyspermy prevention under conditions as physiological as possible. Their kinetic observations in mice gamete interactions challenge present paradigms, as they document that the first sperm is not necessarily the one that fertilizes, suggesting the existence of other post-penetration fertilization factors. The authors find that the zona pellucida (ZP) block triggered by the cortical reaction is too slow to prevent polyspermy in this species. In contrast, their findings indicate that ZP directly contributes to the polyspermy block operating as a naturally effective entry barrier inhibiting the exit from the perivitelline space (PVS) of components released from the oocyte plasma membrane (OPM), neutralizing unwanted sperm fusion, aside from any block caused by fertilization. Furthermore, the authors unveil a new important ZP role regulating flagellar beat in fertilization by promoting sperm fusion in the PVS.

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

SUMMARY: This study by Dubois et al. utilizes live-cell imaging studies of mouse oocytes undergoing fertilization. A strength of this study is their use of three different conditions for analyses of events of fertilization: (1) eggs undergoing fertilization retrieved from females at 15 hr after mating (n = 211 oocytes); (2) cumulus-oocyte complexes inseminated in vitro (n = 220 oocytes), and (3) zona pellucida (ZP)-intact eggs inseminated in vitro, transferred from insemination culture once sperm were observed bound to the ZP for subsequent live-cell imaging (93 oocytes). This dataset and these analyses are valuable for the field of fertilization biology. Limitations of this manuscript are challenges arise with some conclusions, and the presentation of the manuscript. There are some factual errors, and also some places where clearer explanations should to be provided, in the text and potentially augmented with illustrations to provide more clarity on the models that the authors interpret from their data.

MAJOR COMMENTS:

The authors are congratulated on their impressive collection of data from live-cell imaging. However, the writing in several sections is challenging to understand or seems to be of questionable accuracy. The lack of accuracy is suspected to be more an effect of overly ambitious attempts with writing style, rather than to mislead readers. Nevertheless, these aspects of the writing should be corrected. There also are multiple places where the manuscript contradicts itself. These contradictions should be corrected. Finally, there are factual points from previous studies that need correction.

Second, certain claims and the conclusions as presented are not always clearly supported by the data. This may be connected to the issues with writing style, word and phrasing choices, etc. The conclusions could be expressed more clearly, and thus may not require additional experiments or analyses to support them. The authors might also consider illustrations as ways to highlight the points they wish to make. (Figure 7 is a strong example of how they use illustrations to complement the text).

In response to Reviewer 3's concern about the writing style, which made several sections difficult to understand, we have thoroughly revised the entire manuscript to improve clarity, and precision. To further enhance comprehension, we have added illustrations in the revised version of the manuscript:

• Figure 1A presents the gamete components; Figure 1B depicts the main steps of fertilization considered in the present study; and Figure 1C illustrates the penetration and fusion blocks, along with the respective contributing mechanisms: the ZP-block for the penetration block, and the membrane-block and PVS-block for the fusion block

• Figure 2A provides a description of the three experimental protocols used in this study: Condition 1, in vivo fertilization after mating; Condition 2, standard in vitro fertilization following insemination of cumulus-oocyte complexes; and Condition 3, in vitro fertilization with kinetic tracking of oocytes isolated from the insemination medium 15 min after insemination of the cumulus-oocyte complexes.

• Figure 4 (formerly Figure 7 in the initial version) now highlights all fusing and non-fusing situations documented in videos 1-6 and associated paragraphs of the Results section.

• In the Discussion, Figure 9 from the original version has been replaced by Figure 8, which now provides a more pedagogical illustration of the inefficacy of the penetration block in preventing polyspermy in mice. This figure illustrates the respective contributions of the fusion block, the penetration block, fusion timing, and the intrinsic permeability of the zona pellucida to the occurrence of polyspermy.

We hope that this revised version of the article will guide the reader smoothly throughout, without causing confusion.

Regarding the various points that Reviewer 3 perceives as contradictions or factual errors, or the claims and the conclusions which, as presented, should not always supported by the data, we will provide our perspective on each of them as they are raised in the review.

SPECIFIC COMMENTS:

(1) The authors should use greater care in describing the blocks to polyspermy, particularly because they appear to be wishing to reframe views about prevention of polyspermic fertilization. The title mentions of "the fast block to polyspermy;" this problematic for a couple of different reasons. There is no strong evidence for block to polyspermy in mammals that occurs quickly, particularly not in the same time scale as the first-characterized fast block to polyspermy. To many biologists, the term "fast block to polyspermy" refers to the block that has been described in species like sea urchins and frogs, meaning a rapid depolarization of the egg plasma membrane. However, such depolarization events of the egg membrane have not been detected in multiple mammalian species. Moreover, the change in the egg membrane after fertilization does not occur in as fast a time scale as the membrane block in sea urchins and frogs (i.e., is not "fast" per se), and instead occurs in a comparable time frame as the conversation of the ZP associated with the cleavage of ZP2. Thus, it is misleading to use the terms "fast block" and "slow block" when talking about mammalian fertilization. This also is an instance of where the authors contradict themselves in the manuscript, stating, "the membrane block and the ZP block are established in approximatively the same time frame" (third paragraph of Introduction). This statement is indeed accurate, unlike the reference to a fast block to polyspermy in mammals.

We fully agree with Reviewer 3 on the importance of clearly defining the two blocks examined in the present study—the penetration block and the fusion block (as referred to in the revised version) —and of situating them in relation to the three blocks described in the literature: the ZP-block, membrane-block, and PVS-block. We acknowledge that this distinction was not sufficiently clear in the original version of the manuscript. In the revised version, these two blocks and their relationship to the ZP-, membrane-, and PVS-blocks are now clearly introduced in the second paragraph of the Introduction section and illustrated in the first figure of the manuscript (Fig. 1C). They are then discussed in detail in two dedicated paragraphs of the Discussion, entitled Relation between the penetration block and the ZP-block and Relation between the fusion block and the membrane- and PVS-blocks.

The penetration block refers to the time-dependent decrease in the number of spermatozoa penetrating the perivitelline space (PVS) following fertilization, whereas the fusion block refers to the time-dependent decrease in sperm-oolemma fusion events after fertilization. It is precisely to the characterization of these two blocks that our in vitro fertilization experiments with kinetic tracking allow us to access.

In this study, as in the literature, fusion-triggered modifications of the ZP that hinder sperm traversal of the ZP are referred to as the ZP-block (also known as ZP hardening). The ZP-block thus contributes to the post-fertilization reduction in sperm penetration into the PVS and thereby underlies the penetration block. Similarly, fusion-triggered alterations of the PVS and the oolemma that reduce the likelihood of spermatozoa that have reached the PVS successfully to fuse with the oolemma are referred to as the PVS-block and membrane-block, respectively. These two blocks act together to reduce the probability of sperm-oolemma fusion after fertilization, and thus contribute to the fusion block.

The time constant of the penetration block was found to be 48.3 ± 9.7 minutes, which is consistent with the typical timeframe of ZP-block completion—approximately one hour post-fertilization in mice—as reported in the literature. By contrast, the time constant of the fusion block was determined to be 6.2 ± 1.3 minutes, which is markedly faster than the time typically reported in the literature for the completion of the fusion-block (more than one hour in mice). This strongly suggests that the kinetics of the fusion block are not primarily governed by its membrane-block component, but rather by its PVS-block component—about which little to nothing was previously known.

Contrary to what Reviewer 3 appears to have understood from our initial formulation, there is therefore no contradiction or error in stating that "the membrane block and the ZP block are established within approximately the same timeframe", while the fusion block, which proceeds much more rapidly, is likely to rely predominantly on the PVS-block. We have thoroughly revised the manuscript to clarify this key message of the study.

However, we understand Reviewer 3’s objection to referring to the fusion block (or the PVS-block) as a fast block, given that this term is conventionally reserved for the immediate fertilization-triggered membrane depolarization occurring in sea urchins and frogs. Although the kinetics we report for the fusion block are considerably faster than those of the penetration block, they occur on the scale of minutes, and not seconds. In line with the reviewer's recommendation, we have therefore modified both the title and the relevant passages in the text to remove all references to the term fast block in the revised version.

(2) The authors aim to make the case that events occurring in the perivitelline space (PVS) prevent polyspermic fertilization, but the data that they present is not strong enough to make this conclusion. Additional experiments would optional for this study, but data from such additional experiments are needed to support the authors' claims regarding these functions in fertilization. Without additional data, the authors need to be much more conservative in interpretations of their data. The authors have indeed observed phenomena (the presence of CD9 and JUNO in the PVS) that could be consistent with a molecular basis of a means to prevent fertilization by a second sperm. However, the authors would need additional data from additional experimental studies, such as interfering with the release of CD9 and JUNO and showing that this experimental manipulation leads to increased polyspermy, or creating an experimental situation that mimics the presence of CD9 and JUNO (in essence, what the authors call "sperm inhibiting medium" on page 20) and showing that this prevents fertilization.

A major section of the Results section here (starting with "The consequence is that ... ") is speculation. Rather than be in the Results section, this should be in the Discussion. The language should be also softened regarding the roles of these proteins in the perivitelline space in other portions of the manuscript, such as the abstract and the introduction.

Finally, the authors should do more to discuss their results with the results of Miyado et al. (2008), which interestingly, posited that CD9 is released from the oocytes and that this facilitates fertilization by rendering sperm more fusion-competent. There admittedly are two reports that present data that suggest lack of detection of CD9-containing exosomes from eggs (as proposed by Miyado et al.), but nevertheless, the authors should put their results in context with previous findings.

We generally agree with all the remarks and suggestions made here. In the revised version of the manuscript, we have retained in the Results section (pp. 14–15) only the factual data concerning the localization of CD9 and JUNO in unfertilized and fertilized oocytes, as well as in the spermatozoa present in the PVS of these oocytes. We have taken care not to include any interpretive elements in this section, which are now presented exclusively in a dedicated paragraph of the Discussion, entitled “Possible molecular bases of the membrane-block and ZP-block contributing to the fusion block” (p. 21). There, we develop our hypothesis and discuss it in light of both the findings from the present study and previous work by other groups. In doing so, we also address the data reported by Miyado et al. (2008, https://doi.org/10.1073/pnas.0710608105), as well as subsequent studies by two other groups—Gupta et al. (2009, https://doi.org/10.1002/mrd.21040) and Barraud-Lange et al. (2012, https://doi.org/10.1530/REP-12-0040)—that have challenged Miyado’s findings.

We are fully aware that our interpretation of the coverage of unfused sperm heads in the perivitelline space (PVS) by CD9 and JUNO, released from the oolemma—as a potential mechanism of sperm neutralization contributing to the PVS block—remains, at this stage, a plausible hypothesis or working model that, as such, warrants further experimental investigation. It is precisely in this spirit that we present it—first in the abstract (p.1), then in the Discussion section (p. 21), and subsequently in the perspective part of the Conclusion section (p. 22).

(3) Many of the authors' conclusions focus on their prior analyses of sperm interaction - beautifully illustrated in Figure 7. However, the authors need to be cautious in their interpretations of these data and generalizing them to mammalian fertilization as a whole, because mouse and other rodent sperm have sperm head morphology that is quite different from most other mammalian species.

In a similar vein, the authors should be cautious in their interpretations regarding the extension of these results to mammalian species other than mouse, given data on numbers of perivitelline sperm (ranging from 100s in some species to virtually none in other species), suggesting that different species rely on different egg-based blocks to polyspermy to varying extents. While these observations of embryos from natural matings are subject to numerous nuances, they nevertheless suggest that conclusions from mouse might not be able to be extended to all mammalian species.

It is not clear to us whether Reviewer 3’s comment implies that we have, at some point in the manuscript, generalized conclusions obtained in mice to other mammalian species—which we have not—or whether it is simply a general, common-sense remark with which we fully agree: that findings established in one species cannot, by default, be assumed to apply to another.

We would like to emphasize that throughout the manuscript, we have taken care to restrict our interpretations and conclusions to the mouse model, and we have avoided any unwarranted extrapolation to other species.

To definitively close this matter—if there is indeed a matter—we have added the following clarifying statements in the revised version of the manuscript:

In the introduction, second paragraph (pp. 2–3):"The variability across mammalian species in both the rate of fertilized oocytes with additional spermatozoa in their PVS (from 0 to more than 80%) after natural mating and the number of spermatozoa present in the PVS of these oocytes (from 0 to more than a hundred) suggests that the time for completion of the penetration block and thus its efficiency to prevent polyspermy can vary significantly between species."

At the end of the preamble to the Results section (p. 4):"This experimental study was conducted in mice, which are the most widely used model for studying fertilization and polyspermy blocks in mammals. While there are many interspecies similarities, the findings presented here should not be directly extrapolated to humans or other mammalian species without species-specific validation."

In the Conclusion, the first sentence is (p.22) : “This study sheds new light on the complex mechanisms that enable fertilization and ensure monospermy in mouse model.”

Within the Conclusion section, among the perspectives of this work (p. 22):"In parallel, comparative studies in other mammalian species will be needed to assess the generality of the PVS-block and its contribution relative to the membrane-block and ZP-blocks, as well as the generality of the mechanical role played by flagellar beating and ZP mechanical constraint in membrane fusion."

(4) Results, page 4 - It is very valuable that the authors clearly define what they mean by a penetrating spermatozoon and a fertilizing spermatozoon. However, they sometimes appear not to adhere to these definitions in other parts of the manuscript. An example of this is on page 10; the description of penetration of spermatozoon seems to be referring to membrane fusion with the oocyte plasma membrane, which the authors have alternatively called "fertilizing" or fertilization - although this is not entirely clear. The authors should go through all parts of the manuscript very carefully and ensure consistent use of their intended terminology.

Overall, while these definitions on page 4 are valuable, it is still recommended that the authors explicitly state when they are addressing penetration of the ZP and fertilization via fusion of the sperm with the oocyte plasma membrane. This help significantly in comprehension by readers. An example is the section header in the middle of page 9 - this could be "Spermatozoa can penetrate the ZP after the fertilization, but have very low chances to fertilize."

We chose to define our use of the term penetration at the beginning of the Results section because, as readers of fertilization studies, we have encountered on multiple occasions ambiguity as to whether this term was referring to sperm entry into the perivitelline space following zona pellucida traversal, or to the fusion of the sperm with the oolemma. To avoid such ambiguity, we were particularly careful throughout the writing of our original manuscript to use the term penetration exclusively to describe sperm entry into the PVS. The terms fertilizing and fusion were reserved specifically for membrane fusion between the gametes. However, as occasional lapses are always possible, we followed Reviewer 3’s recommendation and carefully re-examined the entire manuscript to ensure consistent use of our intended terminology. We did not identify any inconsistencies, including on page 10, which was cited as an example by Reviewer 3. We therefore confirm that, in accordance with our predefined terminology, all uses of the term penetration, on that page and anywhere else in our original manuscript, refer exclusively to sperm entry into the PVS and do not pertain to fusion with the oolemma.

That said, it is important that all readers— including those who may only consult selected parts of the article—are able to understand it clearly. Therefore, despite the potential risk of slightly overloading the text, Reviewer 3’s suggestion to systematically associate the term penetration with ZP seems to us a sound one. However, we have opted instead to associate penetration with PVS, as our study focuses on the timing of sperm penetration into the perivitelline space, rather than on the traversal of the zona pellucida itself. Accordingly, except in a few rare instances where ambiguity seemed impossible, we have systematically used the phrasing “penetration into the PVS” throughout the revised version of the manuscript.

Another variation of this is in the middle of page 9, where the authors use the terms "fertilization block" and "penetration block." These are not conventional terms, and venture into being jargon, which could leave some readers confused. The authors could clearly define what they mean, particularly with respect to "penetration block,"

This point has already been addressed in our response to Comment 1 from Reviewer 3. We invite Reviewer 3 to refer to that response.

This extends to other portions of the manuscript as well, such as Figure 2C, with the label on the y-axis being "Time after fertilization." It seems that what the authors actually observed here was the cessation of sperm tail motility. (It is not evident they they did an assessment of sperm-oocyte fusion here.)

Regarding Figure 2C (original version), it has been merged with Figure 2B (original version) to form a single figure (Figure S2D), now included in Supplementary Information SI2. This new figure retains all the information originally presented in Figure 2C and indicates the time axis origin as the time when oscillatory movements of the sperm cease.

That said, for the reasons detailed in our response to Reviewer 1 and in the Materials and Methods, we explain why it is legitimate to use the cessation of sperm head oscillations on the oolemma as a marker for the timing of the fusion event. We invite the reviewers to refer to that response for a full explanation of our rationale.

(5) Several points that the authors try to make with several pieces of data do not come across clearly in the text, including Figure 2 on page 6, Figure 4 on page 9, and the various states utilized for the statistical treatment, "post-first penetration, post-first fertilization, no fertilization, penetration block and polyspermy block" on page 10. Either re-writing and clearer definitions'explanations are needed, and/or schematic illustrations could be considered to augment re-written text. Illustrations could be a valuable way present the intended concepts to readers more clearly and accurately. For example, Figure 4 and the associated text on page 9 get particularly confusing - although this sounds like a quite impressive dataset with observations of 138 sperm. Illustrations could be helpful, in the spirit of "a picture is worth 1000 words," to show what seem to be three different situations of sequences of events with the sperm they observed. Finally, the text in the Results about the 138 sperm is quite difficult to follow. It also might help comprehension to augment the percentages with the actual numbers of sperm - e.g., is 48.6% referring 67 of the total 138 sperm analyzed? Does the 85.1% refer to 57 of these 67 sperm?

Figure 2 in the original version of our manuscript concerns sperm engulfment and PB2 extrusion. As already mentioned in our response to Reviewer 1, the characterization of sperm engulfment and PB2 extrusion kinetics is highly relevant to the analysis of the penetration and fusion blocks. However, we agree that its presence in the main text may distract the reader from the main focus of the study. Therefore, this figure and the associated text have been moved to the Supplementary Information in the revised manuscript (SI 2, pages 26–27).

Regarding Figure 4 (original version), in response to Reviewer 3’s concern about the difficulty in grasping the message conveyed in its three graphs and associated text we have completely rethought the way these data are presented. Since the three graphs of Figure 4 were directly derived from the experimental timing data of sperm entry in the PVS and fusion with the oolemma in fertilized oocytes (originally shown in Figure 3A), we have combined them into a single figure in the revised manuscript: Figure 3 (page 8). This new Figure 3 now comprises three components:

• Figure 3A remains unchanged from the original version and shows the timing of sperm penetration and fusion in fertilized oocytes. Each sperm category (fused or non-fused , penetrated in the PVS before fusion or after fusion) is represented using a color code clearly explained in the main text (last paragraph of page 7).
• Figure 3B focuses specifically on the first spermatozoon to penetrate the PVS of each oocyte. It reports how many of these first-penetrating spermatozoa succeeded in fusing versus how many failed to do so, highlighting that being the first to arrive is not sufficient for fusion—other factors are involved. This is explained simply in the first paragraph of page 9.
• Figure 3C considers all spermatozoa that entered the PVS of fertilized oocytes, classifying them into three categories: those that penetrated the PVS before fertilization, those that did so after fertilization, and those for which the timing could not be precisely determined. Such classification makes it apparent that the number of spermatozoa penetrating before and after fertilization is of the same order of magnitude, indicating that fertilization is not very effective at preventing further sperm entry into the PVS for the duration of our observations (~4 hours). To facilitate the identification of these three categories, the same color code used in Figure 3A is applied. In addition, within each category, the number of spermatozoa that successfully fused are indicated in black. This allows the reader to quickly assess the fertilization probability for each category—high for sperm entering before fertilization, very low or null for those entering after fertilization. This analysis shows that fertilization is far more effective at blocking sperm fusion than at blocking sperm penetration. This is clearly explained in the second paragraph of page 9. Regarding__ statistical analysis__, as already mentioned in our responses to Reviewers 1 and 2, this section has been rewritten to improve clarity and readability. The notation has also been significantly simplified. To improve the overall fluidity of the text related to the statistical analysis, Figure 3B (original version), which presented the timing of penetration into the perivitelline space of oocytes that remained unfertilized, along with its associated statistical analysis previously in Figure 5B), have been revised and transferred together in a single Figure S1 of the Supplementary Information (SI1, pages 26; now Figures S1A and S1B).

(6) Introduction, page 2 - it is inaccurate to state that only diploid zygotes can develop into a "new being." Triploid zygotes typically fail early in develop, but can survive and, for example, contribute to molar pregnancies. Additionally, it would be beneficial to be more scientifically precise term than saying "development into a new being." This is recommended not only for scientific accuracy, but also due to current debates, including in lay public circles, about what defines "life" or human life.

In response to Reviewer 3’s comment, we no longer state in the revised version of the manuscript that only diploid zygotes can develop into a new being. We have modified our wording as follows, on page 2, second paragraph: “In mammals, oocytes fertilized by more than one spermatozoon cannot develop into viable offspring.”

(7) Introduction, page 2 - The mammalian sperm must pass through three layers, not just two as stated in the first paragraph of the Introduction. The authors should include the cumulus layer in this list of events of fertilization.

The sentence from the introduction from the original manuscript mentioned by Reviewer 3 was: “To fertilize, a spermatozoon must successively pass two oocyte’s barriers.” This statement is accurate in the sense that the cumulus cell layer is not part of the oocyte itself, unlike the two oocyte’s barriers: the zona pellucida and the oolemma. Moreover, the traversal of the cumulus layer is not within the scope of our study, unlike the traversal of the zona pellucida and fusion with the oolemma. However, it is also correct that in our study the spermatozoa have passed through the cumulus layer before reaching the oocyte. Therefore, in response to Reviewer 3’s comment, we have revised the sentence to clarify this point as follows:

“Once a spermatozoon has passed through the cumulus cell layer surrounding the oocyte, it still must overcome two oocyte’s barriers to complete fertilization.”

(8) Introduction, page 2 - While there is evidence that zinc is released from mouse egg upon fertilization, the evidence is not convincing or conclusive that zinc is released from cortical granules or via cortical granule exocytosis.

To better highlight the rationale, storyline, and scope of our study, the introduction has been thoroughly streamlined. In this context, the section discussing the cortical reaction and zinc release seemed more appropriate in the Discussion, specifically within the paragraph titled “Relationship between the penetration block and the ZP-block.”

To address the uncertainty raised by Reviewer 3 regarding the origin of the zinc spark release, we have rephrased this part as follows:

“The fertilization-triggered processes responsible for the changes in ZP properties are generally attributed to the cortical reaction—a calcium-induced exocytosis of secretory granules (cortical granules) present in the cortex of unfertilized mammalian oocytes—and to zinc sparks. As a result, proteases, glycosidases, lectins, and zinc are released into the perivitelline space (PVS), where they act on the components of the zona pellucida. This leads to a series of modifications collectively referred to as ZP hardening or the ZP-block”.

(9) The authors inaccurately state, "only if monospermic multi-penetrated oocytes are able to develop normally, which to our knowledge has never been proven in mice" (page 4) - This was demonstrated with the Astl knockout, assuming that the authors use of "multi-penetrated oocytes" here refers to the definition of penetration that they use, namely penetrating the ZP. This also is one of the instances where the authors contradict themselves, as they note the results with this knockout on page 18.

Thank you for bringing this point to our attention. Nozawa et al. (2018) found that female mice lacking ovastacin (Astl)—the protease released during the cortical reaction that plays a key role in rendering the zona pellucida impenetrable—are normally fertile. They also reported that oocytes recovered from these females after mating were monospermic, despite the consistent presence of additional spermatozoa in the perivitelline space. We can indeed consider that taken together these findings demonstrate that the presence of multiple spermatozoa in the PVS does not impair normal development, as long as the oocyte remains monospermic. In our study, we re-demonstrated this in a different way (by reimplantation of monospermic oocytes with additional spermatozoa in their PVS) in a more physiological context of WT oocytes, but we agree that we cannot state: “which to our knowledge has never been proven in mice.” This part of the sentence has therefore been removed. In the revised version of the manuscript, the sentence is now formulated in the first paragraph of page 5 as follows: “However, the contribution of the fusion block to prevent polyspermy has physiological significance only if monospermic oocytes with additional spermatozoa in their PVS can develop into viable pups.”

Minor comments:

There are numerous places where this reader marked places of confusion in the text. A sample of some of these:

We will indicate hereinafter how we have modified the text in the specific examples provided by Reviewer 3. Beyond these, however, we would like to emphasize that we have thoroughly revised the entire manuscript to improve clarity and precision.

Page 4 - "continuously relayed by other if they detach" - don't know what this means

Replaced now p 5 by “can be replaced by others if they detach”

Page 6 - "hernia" - do the authors mean "protrusion" on the oocyte surface?

The paragraph from the Results section in question has now been moved to the Supplementary Information, on pages 26 and 27. The term hernia has been systematically replaced with protrusion, including in the Materials and Methods section on page 24.

Page 10 - "penetration of spermatozoa in the PVS falls down" - don't know what this means

Falls down has been removed from the new version and replaced with decreases

Page 12 - "spermatozoa linked to the oocyte ZP" - not clear what "linked" means here

Replaced now page 16 by “spermatozoa bound to the oocyte ZP”

Page 14 - "by dint of oscillations" - don't know what this means

Replaced now page 10 by “the persistent flagellum movements”

Specifics for Materials and Methods:

Exact timing of females receiving hCG and then being put with males for mating - assume this was immediate but this is an important detail regarding the timing for the creation of embryos in vivo.

That is correct: females were placed with males for mating immediately after receiving hCG. This clarification has been added in the revised version of the manuscript.

Please provide the volumes in which inseminations occurred, and how many eggs were placed in this volume with the 10^6 sperm/ml.

The number of eggs may vary from one cumulus–oocyte complex to another. It is therefore not possible to specify exactly how many eggs were inseminated. However, we now indicate on page 23 the number of cumulus–oocyte complexes inseminated (4 per experiment), the volume in which insemination was performed (200 mL), and the sperm concentration used 106 sperm/mL.

**Referees cross-commenting**

I concur with Reviewer 1's comment, that the 'challenging prior dogma' about the first sperm not always being the one to fertilize the egg is too strong. As Reviewer 1 notes, "it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg." I even thought about adding this comment to my review, although held off (I was hoping to find references, but that was taking too long).

Please refer to our response to Reviewer 1 regarding this point.

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:

This study by Dubois et al. utilizes live-cell imaging studies of mouse oocytes undergoing fertilization. A strength of this study is their use of three different conditions for analyses of events of fertilization: (1) eggs undergoing fertilization retrieved from females at 15 hr after mating (n = 211 oocytes); (2) cumulus-oocyte complexes inseminated in vitro (n = 220 oocytes), and (3) zona pellucida (ZP)-intact eggs inseminated in vitro, transferred from insemination culture once sperm were observed bound to the ZP for subsequent live-cell imaging (93 oocytes). This dataset and these analyses are valuable for the field of fertilization biology. Limitations of this manuscript are challenges arise with some conclusions, and the presentation of the manuscript. There are some factual errors, and also some places where clearer explanations should to be provided, in the text and potentially augmented with illustrations to provide more clarity on the models that the authors interpret from their data.

Major comments:

The authors are congratulated on their impressive collection of data from live-cell imaging. However, the writing in several sections is challenging to understand or seems to be of questionable accuracy. The lack of accuracy is suspected to be more an effect of overly ambitious attempts with writing style, rather than to mislead readers. Nevertheless, these aspects of the writing should be corrected. There also are multiple places where the manuscript contradicts itself. These contradictions should be corrected. Finally, there are factual points from previous studies that need correction.

Second, certain claims and the conclusions as presented are not always clearly supported by the data. This may be connected to the issues with writing style, word and phrasing choices, etc. The conclusions could be expressed more clearly, and thus may not require additional experiments or analyses to support them. The authors might also consider illustrations as ways to highlight the points they wish to make. (Figure 7 is a strong example of how they use illustrations to complement the text).

Specific comments:

1. The authors should use greater care in describing the blocks to polyspermy, particularly because they appear to be wishing to reframe views about prevention of polyspermic fertilization. The title mentions of "the fast block to polyspermy;" this problematic for a couple of different reasons. There is no strong evidence for block to polyspermy in mammals that occurs quickly, particularly not in the same time scale as the first-characterized fast block to polyspermy. To many biologists, the term "fast block to polyspermy" refers to the block that has been described in species like sea urchins and frogs, meaning a rapid depolarization of the egg plasma membrane. However, such depolarization events of the egg membrane have not been detected in multiple mammalian species. Moreover, the change in the egg membrane after fertilization does not occur in as fast a time scale as the membrane block in sea urchins and frogs (i.e., is not "fast" per se), and instead occurs in a comparable time frame as the conversation of the ZP associated with the cleavage of ZP2. Thus, it is misleading to use the terms "fast block" and "slow block" when talking about mammalian fertilization.

This also is an instance of where the authors contradict themselves in the manuscript, stating, "the membrane block and the ZP block are established in approximatively the same time frame" (third paragraph of Introduction). This statement is indeed accurate, unlike the reference to a fast block to polyspermy in mammals.<br /> 2. The authors aim to make the case that events occurring in the perivitelline space (PVS) prevent polyspermic fertilization, but the data that they present is not strong enough to make this conclusion. Additional experiments would optional for this study, but data from such additional experiments are needed to support the authors' claims regarding these functions in fertilization. Without additional data, the authors need to be much more conservative in interpretations of their data. The authors have indeed observed phenomena (the presence of CD9 and JUNO in the PVS) that could be consistent with a molecular basis of a means to prevent fertilization by a second sperm. However, the authors would need additional data from additional experimental studies, such as interfering with the release of CD9 and JUNO and showing that this experimental manipulation leads to increased polyspermy, or creating an experimental situation that mimics the presence of CD9 and JUNO (in essence, what the authors call "sperm inhibiting medium" on page 20) and showing that this prevents fertilization.

A major section of the Results section here (starting with "The consequence is that ... ") is speculation. Rather than be in the Results section, this should be in the Discussion. The language should be also softened regarding the roles of these proteins in the perivitelline space in other portions of the manuscript, such as the abstract and the introduction.

Finally, the authors should do more to discuss their results with the results of Miyado et al. (2008), which interestingly, posited that CD9 is released from the oocytes and that this facilitates fertilization by rendering sperm more fusion-competent. There admittedly are two reports that present data that suggest lack of detection of CD9-containing exosomes from eggs (as proposed by Miyado et al.), but nevertheless, the authors should put their results in context with previous findings. 3. Many of the authors' conclusions focus on their prior analyses of sperm interaction - beautifully illustrated in Figure 7. However, the authors need to be cautious in their interpretations of these data and generalizing them to mammalian fertilization as a whole, because mouse and other rodent sperm have sperm head morphology that is quite different from most other mammalian species.

In a similar vein, the authors should be cautious in their interpretations regarding the extension of these results to mammalian species other than mouse, given data on numbers of perivitelline sperm (ranging from 100s in some species to virtually none in other species), suggesting that different species rely on different egg-based blocks to polyspermy to varying extents. While these observations of embryos from natural matings are subject to numerous nuances, they nevertheless suggest that conclusions from mouse might not be able to be extended to all mammalian species.<br /> 4. Results, page 4 - It is very valuable that the authors clearly define what they mean by a penetrating spermatozoon and a fertilizing spermatozoon. However, they sometimes appear not to adhere to these definitions in other parts of the manuscript. An example of this is on page 10; the description of penetration of spermatozoon seems to be referring to membrane fusion with the oocyte plasma membrane, which the authors have alternatively called "fertilizing" or fertilization - although this is not entirely clear. The authors should go through all parts of the manuscript very carefully and ensure consistent use of their intended terminology.

Overall, while these definitions on page 4 are valuable, it is still recommended that the authors explicitly state when they are addressing penetration of the ZP and fertilization via fusion of the sperm with the oocyte plasma membrane. This help significantly in comprehension by readers. An example is the section header in the middle of page 9 - this could be "Spermatozoa can penetrate the ZP after the fertilization, but have very low chances to fertilize."

Another variation of this is in the middle of page 9, where the authors use the terms "fertilization block" and "penetration block." These are not conventional terms, and venture into being jargon, which could leave some readers confused. The authors could clearly define what they mean, particularly with respect to "penetration block,"

This extends to other portions of the manuscript as well, such as Figure 2C, with the label on the y-axis being "Time after fertilization." It seems that what the authors actually observed here was the cessation of sperm tail motility. (It is not evident they they did an assessment of sperm-oocyte fusion here.) 5. Several points that the authors try to make with several pieces of data do not come across clearly in the text, including Figure 2 on page 6, Figure 4 on page 9, and the various states utilized for the statistical treatment, "post-first penetration, post-first fertilization, no fertilization, penetration block and polyspermy block" on page 10 . Either re-writing and clearer definitions'explanations are needed, and/or schematic illustrations could be considered to augment re-written text. Illustrations could be a valuable way present the intended concepts to readers more clearly and accurately. For example, Figure 4 and the associated text on page 9 get particularly confusing - although this sounds like a quite impressive dataset with observations of 138 sperm. Illustrations could be helpful, in the spirit of "a picture is worth 1000 words," to show what seem to be three different situations of sequences of events with the sperm they observed. Finally, the text in the Results about the 138 sperm is quite difficult to follow. It also might help comprehension to augment the percentages with the actual numbers of sperm - e.g., is 48.6% referring 67 of the total 138 sperm analyzed? Does the 85.1% refer to 57 of these 67 sperm?<br /> 6. Introduction, page 2 - it is inaccurate to state that only diploid zygotes can develop into a "new being." Triploid zygotes typically fail early in develop, but can survive and, for example, contribute to molar pregnancies. Additionally, it would be beneficial to be more scientifically precise term than saying "development into a new being." This is recommended not only for scientific accuracy, but also due to current debates, including in lay public circles, about what defines "life" or human life. <br /> 7. Introduction, page 2 - The mammalian sperm must pass through three layers, not just two as stated in the first paragraph of the Introduction. The authors should include the cumulus layer in this list of events of fertilization. 8. Introduction, page 2 - While there is evidence that zinc is released from mouse egg upon fertilization, the evidence is not convincing or conclusive that zinc is released from cortical granules or via cortical granule exocytosis.<br /> 9. The authors inaccurately state, "only if monospermic multi-penetrated oocytes are able to develop normally, which to our knowledge has never been proven in mice" (page 4) - This was demonstrated with the Astl knockout, assuming that the authors use of "multi-penetrated oocytes" here refers to the definition of penetration that they use, namely penetrating the ZP. This also is one of the instances where the authors contradict themselves, as they note the results with this knockout on page 18.

Minor comments:

There are numerous places where this reader marked places of confusion in the text. A sample of some of these:

Page 4 - "continuously relayed by other if they detach" - don't know what this means

Page 6 - "hernia" - do the authors mean "protrusion" on the oocyte surface?

Page 10 - "penetration of spermatozoa in the PVS falls down" - don't know what this means

Page 12 - "spermatozoa linked to the oocyte ZP" - not clear what "linked" means here

Page 14 - "by dint of oscillations" - don't know what this means

Specifics for Materials and Methods:

Exact timing of females receiving hCG and then being put with males for mating - assume this was immediate but this is an important detail regarding the timing for the creation of embryos in vivo.

Please provide the volumes in which inseminations occurred, and how many eggs were placed in this volume with the 10^6 sperm/ml.

Referees cross-commenting

I concur with Reviewer 1's comment, that the 'challenging prior dogma' about the first sperm not always being the one to fertilize the egg is too strong. As Reviewer 1 notes, "it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg." I even thought about adding this comment to my review, although held off (I was hoping to find references, but that was taking too long).

Significance

This manuscript brings interesting new observations for the field of gamete and fertilization biology. For very obvious reasons, the understanding of mammalian fertilization has lagged behind the understanding of fertilization of species with external fertilization. Decades ago, developmental biologists first focused on studies of fertilization on gametes from species that release sperm and egg into water, either spontaneously or with relatively easy stimulation, and gametes that could be easily cultured and enabled to create embryos as researchers watched. Studies of mammalian fertilization have since caught up, with the elucidation of conditions that support in vitro fertilization in various mammalian species, most notably mouse as an experimental model.

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Referee #2

Evidence, reproducibility and clarity

Overall, this is a very interesting and relevant work for the field of fertilization. In general, the experimental strategies are adequate and well carried out. I have some questions and suggestions that should be considered before the work is published.

1. Why are the cumulus cells not mentioned when the AR is triggered before or while the sperms cross it? It seems the paper assumes from previous work that all sperm that reach ZP and the OPM have carried out the acrosome reaction. This, though probably correct, is still a matter of controversy and should be discussed. It is in a way strange that the authors do not make some controls using sperm from mice expressing GFP in the acrosome, as they have used in their previous work.
2. In the penetration block equations, it is not clear to me why (𝑡𝑃𝐹1) refers to both PIPF1 and 𝜎𝜎𝑃I𝑃𝐹1. Is it as function off?
3. Why do the authors think that the flagella stops. The submission date was 2024-10-01 07:27:26 and there has been a paper in biorxiv for a while that merits mention and discussion in this work (bioRxiv [Preprint]. 2024 Jul 2:2023.06.22.546073. doi: 10.1101/2023.06.22.546073.PMID: 37904966).
4. Please correct at the beginning of Materials and Methos: Sperm was obtained from WT male mice, it should say were.
5. This is also the case in the fourth paragraph of this section: oocyte were not was.

Significance

Understanding mammalian gamete fusion and polyspermy inhibition has not been fully achieved. The authors examined real time brightfield and confocal images of inseminated ZP-intact mouse oocytes and used statistical analyses to accurately determine the dynamics of the events that lead to fusion and involve polyspermy prevention under conditions as physiological as possible. Their kinetic observations in mice gamete interactions challenge present paradigms, as they document that the first sperm is not necessarily the one that fertilizes, suggesting the existence of other post-penetration fertilization factors. The authors find that the zona pellucida (ZP) block triggered by the cortical reaction is too slow to prevent polyspermy in this species. In contrast, their findings indicate that ZP directly contributes to the polyspermy block operating as a naturally effective entry barrier inhibiting the exit from the perivitelline space (PVS) of components released from the oocyte plasma membrane (OPM), neutralizing unwanted sperm fusion, aside from any block caused by fertilization. Furthermore, the authors unveil a new important ZP role regulating flagellar beat in fertilization by promoting sperm fusion in the PVS.

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Referee #1

Evidence, reproducibility and clarity

The manuscript "Key roles of the zona pellucida and perivitelline space in promoting gamete fusion and fast block to polyspermy inferred from the choreography of spermatozoa in mice oocytes" by Dr. Gourier and colleagues explores the poorly understood process of gamete fusion and the subsequent block to polyspermy by live-cell imaging of mouse oocytes with intact zona pellucida in vitro. The new component in this study is the presence of the ZP, which in prior studies of live-cell imaging had been removed before. This allowed the authos to examine contributions of the ZP to the block in polyspermy in relation to the timing of sperm penetrating the ZP and sperm fusing with the oocyte. By carefully analysing the timing of the cascade of events, the authors find that the first sperm that reaches the membrane of the mouse oocyte is not necessarily the one that fertilizes the oocytes, revealing that other mechanisms post-ZP-penetration influence the success of individual sperm. While the rate of ZP penetration remains constant in unfertilized oocytes, it decreases upon fertilization for subsequent sperm, providing direct evidence for the known 'slow block to polyspermy' provided by changes to the ZP adhesion/ability to be penetrated. Careful statistical analyses allow the authors to revisit the role of the ZP in preventing polyspermy: They show that the ZP block resulting from the cortical reaction is too slow (in the range of an hour) to contribute to the immediate prevention of polyspermy in mice. The presented analyses reveal that the ZP does contribute to the block to polyspermy in two other ways, namely by effectively limiting the number of sperm that reach the oocyte surface in a fertilization-independent manner, and by retaining components like JUNO and CD9, that are shed from the oocyte plasma membrane after fertilization, in the perivitelline space, which may help neutralize surplus spermatozoa that are already present in the PVS. Lastly, the authors report that the ZP may also contribute to channeling the flagellar oscillations of spermatozoa in the PVS to promote their fusion competence.

Major comments:

• Are the key conclusions convincing?

The authors provide a careful analysis of the dynamics of events, though the analyses are correlative, and can only be suggestive of causation. While this is a limitation of the study, it provides important analysis for future research. Moreover, by analysing also control oocytes without fertilization and the timing of events, the authors have in some instances clear 'negative controls' for comparison.

Some claims would benefit from rewording or rephrasing to put the findings better in the context of what is already known and what is novel: - the phrasing 'challenging prior dogma' might be too strong since it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg (though I am afraid that I do not have any citations or references for this). However, given that in the field people generally think it is not necessarily and always the first sperm, the authors may want to consider weakening this claim. - I do think the cortical granule release could still contribute to the block to polyspermy though - as the authors here nicely show - at a later time-point only, and thus not the major and not the immediate block as previously thought. The wording in the abstract should therefore be adjusted (since it could still contribute...) - the finding that the ZP presents a natural effective barrier for sperm entry is not that novel (as suggested here) - there are mutants that prevent sperm from getting through the ZP and thus to the oocyte and those lead to sterility - release of OPM components - in the abstract it's unclear what the authors mean by this - in the results part it becomes clear. Please already make it clear in the abstract that it is the fertility factors JUNO/CD9 that could bind to sperm heads upon their release and thus 'neutralize' them? I would also recommend not referring to it as 'outer' plasma membrane (there is no 'inner plasma membrane'). Moreover, in the abstract please clarify that this release is happening only after fusion of the first sperm and not all the time. In the abstract it sounds as if this was a completely new idea, but there is good prior evidence that this is in fact happening (as also then cited in the results part) - maybe frame it more as the retention inside the PVS as new finding.

It is unclear to me what the relevance of dividing the post-fusion/post-engulfment into different phases as done in Fig 2 (phase 1, and phase 2) - also for the conclusions of this paper this seems rather irrelevant and overly complicated, since the authors never get back to it and don't need it (it's not related to the polyspermy block analyses). I would remove it from the main figures and not divide into those phases since it is distracting from the main focus.

For the statistical analysis, I am not sure whether the assumption "assumption that the probability distribution of penetration or fertilization is uniform within a given time window" is in fact true since the probability of fertilizing decreases after the first fertilization event.... Maybe I misunderstood this, but this needs to be explained (or clarified) better, or the limitation of this assumption needs to be highlighted. - Suggestion for additional experiments:

If I understood correctly, the onset of fusion in Fig 2C is defined by stopping of sperm beating? If it is by the sudden stop of the beating flagellum, this should be confirmed in this situation (with the ZP intact) that it correctly defines the time-point of fusion since this has not been measured in this set-up before as far as I understand. In order to measure this accurately, the authors will need to measure this accurate to be able to acquire those numbers (of time from fusion to end of engulfment), e.g. by pre-loading the oocyte with Hoechst to transfer Hoechst to the fusing sperm upon membrane fusion.

Fig 8: 2 comments - To better show JUNO/CD9 pre-fusion attachment to the oocyte surface and post-fusion loss from the oocyte surface (but persistence in the PVS), an image after removal of the ZP (both for pre-fertilization and post-fertilization) would be helpful - the combination of those images with the ones you have (ZP intact) would make your point more visible. - You show that the heads of spermatozoa post fusion are covered in CD9 and JUNO, yet I was missing an image of sperm in the PVS pre-fertilization (which should then not yet be covered).

Minor comments:

• The videos were remarkable to look at, and great to view in full. However, for the sake of time, the authors might want to consider cropping them for the individual phases to have a shorter video (with clear crop indicators) with the most important different stages visible in a for example 1 min video (e.g. video 1)
• In general, given that the ZP, PVS and oocyte membrane are important components, a general scheme at the very beginning outlining the relative positioning of each before and during fertilization (and then possibly also including the second polar body release) would be extremely helpful for the reader to orient themselves.
• first header results "Multi-penetration and polyspermy under in vivo conditions and standard and kinetics in vitro fertilization conditions" is hard to understand - simplify/make clearer (comparison of in vivo and in vitro conditions? Establishing the in vitro condition as assay?)
• Large parts of the statistical analysis (the more technical parts) could be moved to the methods part since it disrupts the flow of the text.
• To me, one of the main conclusions was given in the text of the results part, namely that "This suggests that first fertilization contributes effectively to the fertilization
• block, but less so to the penetration block". I would suggest that the authors use this conclusion to strengthen their rationale and storyline in the abstract.
• Wording: To characterize the kinetics with which penetration of spermatozoa in the PVS falls down after a first fertilization," falls down should be replaced with decreases (page 10 and page 12)

Significance

Overall, this manuscript provides very interesting and carefully obtained data which provides important new insights particularly for reproductive biology. I applaud the authors on first establishing the in vivo conditions (how often do multiple sperm even penetrate the ZP in vivo) since studies have usually just started with in vitro condition where sperm at much higher concentration is added to isolated oocyte complexes. Thank you for providing an in vivo benchmark for the frequency of multiple sperm being in the PVS. While this frequency is rather low (somewhat expectedly, with 16% showing 2-3 sperm in the PVS), this condition clearly exists, providing a clear rationale for the investigation of mechanisms that can prevent additional sperm from entering.

My own expertise is experimentally - thus I don't have sufficient expertise to evaluate the statistical methods employed here.

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Reply to the reviewers

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

The authors use Dyngo-4a, a known Dynami inhibitor to test its influence on caveolar assembly and surface mobility. They investigate, whether it incorporates into membranes with Quartz-Crystal Microbalance, they investigate how it is organized in membranes using simulations. Finally, they use lipid-packing sensitive dyes to investigate lipid packing in the presence of Dyngo-4a, membrane stiffness using AFM and membrane undulation using fluorescence microscopy. They also use a measure they call "caveola duration time" to claim that something happens to caveolae after Dyngo-4a addition and using this parameter, they do indeed see an increase in it in response to Dyngo-4a, which is reduced back to the baseline after addition of cholesterol.

Overall, the authors claim: 1) Dyngo-4a inserts into the membrane and this 2) results in "a dramatic dynamin-independent inhibition of caveola scission". 3) Dyngo-4a was inserted and positioned at the level of cholesterol in the bilayer and 4) Dyngo-4a-treatment resulted in decreased lipid packing in the outer leaflet of the plasma membrane 5) but Dyngo-4a did not affect caveola morphology, caveolae- associated proteins, or the overall membrane stiffness 6) acute addition of cholesterol counteracts the block in caveola scission caused by Dyngo-4a

Overall, in this reviewers opinion, claims 1, 3, 4, 5 are well-supported by the presented data from electron and live cell microscopy, QCM-D and AFM. However, there is no convincing assay for caveolar endocytosis presented besides the "caveola duration" which although unclearly described seems to be the time it takes in imaging until a caveolae is not picked up by the tracking software anymore in TIRF microscopy. Since the main claim of the paper is a mechanism of caveolar endocytosis being blocked by Dyngo-4a, a true caveolar internalization assays is required to make this claim. This means either the intracellular detection of not surface connected caveolar cargo or the quantification of caveolar movement from TIRF into epifluorescence detection in the fluorescence microscope. Otherwise, the authors could remove the claim and just claim that caveolar mobility is influenced.

Response: We thank the reviewer for the nice constructive comments, and we very much appreciate the positive critique. We have now included a FRAP experiment of endocytic Cav1-GFP supporting the effect on internalization. In addition, we are currently preforming CTxB HRP experiments to quantify the number of caveolae at PM using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long.

Reviewer #1 (Significance (Required)):

A number of small molecule inhibitors for the GTPase dynamics exist, that are commonly used tools in the investigation of endocytosis. This goes as far that the use of some of these inhibitors alone is considered in some publications as sufficient to declare a process to be dynamin-dependent. However, this is not correct, as there are considerable off-target effects, including the inhibition of caveolar internalization by a dynamin-independent mechanism. This is important, as for example the influence of dynamin small molecule inhibitors on chemotherapy resistance is currently investigated (see for example Tremblay et al., Nature Communications, 2020).

The investigation of the true effect of small molecules discovered as and used as specific inhibitors and their offside effects is extremely important and this reviewer applauds the effort. It is important that inhibitors are not used alone, but other means of targeting a mechanism are exploited as well in functional studies. The audience here thus is besides membrane biophysicists interested in the immediate effect of the small molecule Dyngo-4a also cell biologists and everyone using dynamic inhibitors to investigate cellular function.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

This manuscript uses the small molecule dynamin inhibitors dynasore and dyngo to show that in dynamin triple knockout cells that these inhibitors impact lipid packing and organization in the plasma membrane. Data showing that dyngo affects caveolin dynamics using tirf microscopy is also shown and is interpreted to reflect inhibition of caveolae scission from the membrane.

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane. What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane. Study of caveolae endocytosis is based on a TIRF assay that has inherent limitations: - Caveolae are defined as bright cav1-positive spots in diffraction limited TIRF and their disappearance presumed to be endocytic events. Cav1 spots are presumed to be caveolae but the authors do not consider that they may be flat non-caveolar oligomers. The diffraction limited TIRF approach interprets the large structures as caveolae but evidence to that effect is lacking.

Response: This is a valid comment and to address this we have now included data showing colocalization of cavin1 and EHD2 to the Cav1-GFP spots. We can however not determine if they are flat or invaginated. We do have extensive experience imaging caveolae using TIRF microscopy and carefully chose cells that display low expression of fluorescently labelled caveolin to avoid non-caveolar structures.

• The analysis (and the diagram presented in figure 4) considers that caveolae can either diffuse laterally in the membrane or internalize and does not consider that caveolae can flatten and possibly fragment in the membrane. Is it not possible that loss of Cav1 spots is a fragmentation event and not necessarily a scission event?

Response: This is a good question, yet, fragmentation and disassembly would result in shorter track durations and this is not what is observed in data. We have now also included data showing that cavin1 is persistently associated with the Cav1 spots identified as caveolae during Dyngo-4a treatment indicating that these are caveolae. Furthermore, IF stainings showing colocalization of Cav1GFP with cavin1 or EHD2 after Dyngo-4a treatment have also been added. We have now also expanded on the different interpretations of the data in the results section.

• The analysis is based on overexpression of Cav1-GFP that may alter the stoichiometry between Cav1 and cavin1 such that while caveolae may be expressed, larger non-caveolar structures may accumulate.

Response: Yes, this is correct, we have specifically imaged cell expressing low levels of Cav1-GFP to avoid accumulated non-caveolar structures that can be spotted in cells with high expression.

• Cav1 has been shown to be internalized via the CLIC pathway (Chaudary et al, 2014) and if dyngo is impacting clathrin then maybe it is also impacting CLIC endocytosis and thereby Cav1 endocytosis via this pathway?

Response: Dyngo-4a has been shown to not affect CLIC endocytosis (McCluskey et al., 2013) and in our data we do not see internalization following Dyngo-4a treatment.

• The longer Cav1 TIRF track time and shorter displacement with dyngo is consistent with inhibition of caveolae scission. However, as the authors discuss, could not reduced membrane undulations due to dyngo's impact on membrane order be responsible for the longer tracks? Alternatively, perhaps the altered lipid packing is corralling Cav1 movement and reducing non-caveolar Cav1 endocytosis, resulting in shorter tracks of longer duration? The proposed interaction of dyngo with cholesterol could prevent scission but also stabilize large (flat?) Cav1 oligomers in the membrane, perhaps reducing Cav1 oligomer fragmentation.

Response: We completely agree that membrane undulations contribute to instability of the TIRF-field and therefore disruption of cav1-GFP tracks as we discuss in the results section and have been described in previous work (Larsson et al., 2023). Yet, we have also shown that internalization of caveolae results in shorter tracks (Hubert et al., 2020; Larsson et al., 2023; Mohan et al., 2015). Furthermore, the tracked Cav1-GFP spots are persistently positive for cavin1 both with and without Dyngo-4a treatment showing that the majority do not disassemble become internalized by other pathways. Additionally, the added IF stainings after 30 min Dyngo-4a treatment also show that the Cav1-GFP spots remain positive for cavin1 and EHD2 just as ctrl-treated cells.

My point here is not to discredit the data but only to suggest that the TIRF approach used is an indirect measure of caveolae scission from the membrane that requires substantiation using other approaches.

Response: We appreciate these comments and have tried to address these by adding new data and discussions on the interpretation of the tracking data in the results section.

Dyngo is certainly generally affecting lipid packing via cholesterol and thereby affecting Cav1 dynamics in the plasma membrane. The claim of caveolae scission should be qualified and alternative possibilities considered and discussed. If the authors persist in arguing that dyngo is affecting caveolae scission then the effect should be substantiated by accumulation of caveolae by quantitative EM and high spatial and temporal resolution imaging of Cav1 and cavin1 to define the endocytic events. As the latter represents a new, and potentially very challenging, line of experimentation, I would suggest that it is beyond the scope of the current study. As indicated above the additional experiments are not necessary and qualification of the claims would be sufficient.

-Response: We have now included a FRAP experiment of endocytic Cav1-GFP supporting the effect on internalization. We are also currently preforming CTxB HRP experiments to quantify the number of caveolae at the PM using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long.

Other points

Figure 1C - Cav1 positive spots cannot be interpreted to be caveolae from diffraction limited confocal images. Same comment applies to Fig 4G - caveola? duration.

-Response: We completely agree with this and that the claims should be qualified. We have added IF stainings showing that the Cav1-GFP structures are also positive for cavin1. We have now clarified that we cannot distinguish between flat or different curved states of caveolae using this methodology. We have also changed the labelling of Fig. 4G.

Figure 4C - it is not clear why this EM data is not quantified - for both the number of caveolae and clathrin coated pits - as this would help clarify the interpretation of the effect reported.

-Response: We are currently preforming CTxB HRP experiments to quantify the number of caveolae using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long.

Figure 4D - the AFM experiments should perhaps be repeated as the non-significant effect of dyngo on the Young's modulus may be a result of insufficient n values. -Response: We would like to clarify that to ensure the robustness of our AFM measurements, we performed the experiments with sufficient biological and technical replicates. Specifically, each data point shown in Figure 4D represents a Young’s modulus value averaged from approximately sixty force-distance curves per cell. For each condition, we collected force-distance maps on eight to nine individual cells, obtained from two separate petri dishes per day. We repeated this process on two independent days. In total, we analysed thirty-one cells for the DMSO control and thirty-three cells for the Dyngo-4a treatment. We performed the “student’s t-test with Welch’s correction” to access the statistical significance between the two conditions, as described in the main text. We believe that the sample size and statistical approach are sufficient to support the conclusions presented. Furthermore, we also analysed cell stiffness by calculating the slope of the linear portion of the force-distance curves. This analysis also did not reveal any statistically significant differences between the conditions (data not shown), further supporting our conclusion that Dyngo-4a treatment does not significantly alter the Young’s modulus under our experimental setup (or conditions).

Reviewer #2 (Significance (Required)):

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane. What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane.

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

Larsson et al present experimental and computational data on the role of Dyngo4a (a compound that was developed to inhibit dynamin) on the dynamics of caveolae. The manuscript mostly documents effects of Dyngo on caveolae, with one experiment to suggest a mechanism for this result. This one rather unconvincing result forms the focus of the manuscript contributing to a disconnect between the data and the presentation. Additionally, there are concerns with data interpretation. The writing could also benefit from revision to address grammar mistakes, strengthen referencing, and increase precision. Overall, the manuscript requires substantial revisions before being considered for publication. The central claim, in particular, needs stronger evidence to support the proposed mechanism. -Response: We thank the reviewer for the thorough review and for experimental suggestions that we believe has strengthened our data further.

Significant issues (in approximate order of importance): 1. The data supporting the central mechanistic explanation appears limited. There is no evidence that Dyngo remains in one leaflet

Response:The simulations show that the energy barrier for moving in between bilayers is very high. Furthermore, simulations of C-Laurdan has shown that it does not readily flip in between membrane leaflets (Barucha-Kraszewska et al., 2013) supporting that it reports on the outer lipid leaflet when added to cells. We have however now changed this and state that Dyngo-4a decreased the lipid order in the plasma membrane.

the GP of the PM is very low compared to previous measurements,

Response: The absolute GP-values will vary between setups depending on what filters are used so they are not comparable between laboratories. What is of importance is that we found a significant change in the relative GP-values in cells treated with Dyngo-4a and control cells. It is this change that we report. We have not performed any GP-measurements on this cell type earlier so it is unclear what previous measurements reviewer #3 are referring to.

effects on other membranes are not explored,

Response: The order of the intracellular membranes is as expected lower than that of the plasma membrane. Differentiating different intracellular membranes of interest like endocytotic vesicles from other intracellular membranes would be very difficult but, more importantly, our study is focused on what is happening in the plasma membrane where caveolae reside and would be of minor interest for plasma membrane dynamics.

dynamin-directed effects of Dyngo are not considered,

Response: In the discussion section we discuss the difficulties with disentangling dynamin-direct and indirect effects.

The QCM-D measurements and claims require explanation as several aspects remains unclear. In Fig S2, the 'softness' (what does this mean?) changes by 4-fold with DMSO alone (what does this mean?), then fractionally more with Dyngo. Then fractionally more again when Dyngo is removed (why?). Then it remains somewhat higher when both Dyngo and DMSO are removed, which is somehow interpreted as Dyngo remaining in the bilayer, but not DMSO.

Response:We understand the confusion of the reviewer and hope our explanations provide clarity. QCM-D measurements are based on an oscillating quartz crystal sensor. Specifically, alterations in oscillation frequency (ΔF) and the rate of energy dissipation from the sensor surface (ΔD) are what is measured. Allowing the measurement of: 1) materials adsorbing to the sensor surface, 2) changes in the viscoelastic properties of a solution in contact with the sensor surface, 3) changes in the material adsorbed to the sensor surface upone exposure to different solutions. The ratio of ΔD/-ΔF reports the mechanical softness or rigidity of an adsorbed material, in this case the SLB.A “buffer shift” is the term used when there is not an adsorption to the sensor surface, but rather an effect from altering the solution above the sensor surface. One reason is because different solutions can have different densities (e.g., a DMSO-buffer mixture vs buffer alone), which impacts the oscillations of the sensor. It was observed that the DMSO-buffer mixture alone gave a large buffer shift in comparison to the adsorption of the Dyngo-4a into the SLB, thereby muddling the data interpretation. Thus, in Fig. S2 the system was first equilibrated with the DMSO-buffer mixture prior to addition of the Dyngo-4a solution to allow for clearer visualization of the two events. In QCMD to assess if something has made a permeant change to the system you change back to the solutions used before the addition, thus first we washed with a DMSO-Buffer mixture followed by buffer alone. Control experiments were carried out in which no Dyngo-4a was added (also shown in Fig. S2). The control shows the same “buffer shift” from the DMSO-buffer mixture occurs in both systems and that upon returning to a buffer only condition there is no permanent change to the system caused from exposure to the DMSO. In contrast, once the system that received Dyngo-4a is changes back to a buffer only system we see that mass has been added to the system (ΔF) with little change to the dissipation (ΔD), thereby resulting in a lower ratio of ΔD/-ΔF, which is to say that the SLB after the adsorption of Dyngo-4a was more rigid that the SLB without Dyngo-4a.

These interpretations are difficult to grasp, as the authors seem to be implying simple amphiphilic partitioning into the membrane, which should all be removable by efficient washing.

Response: Amphiphilic partitioning is not fully reversible by “efficient washing” it depends on partitioning coefficients.

I do not doubt that this compound interacts with membranes, but the quantifications appear ambiguous. A bilayer with 16 mol% (or worse, 30% if all in one leaflet) Dyngo is very unlikely (to remain a bilayer). Even if such a bilayer was conceivable, the authors are claiming an ADDITION of Dyngo that would INCREASE the area of one leaflet by 30%, which needs explanation as it appears unlikely.

-Response: We understand that in our attempt provide numbers in the results section for the amount of binding observed in QCM-D, this can easily be interpreted as this is what is observed to insert into the PM. However, as discussed in the discussion, we also see aggregations of Dyngo-4a that associate with the membrane in the simulations which likely could contribute to the binding observed in QCM-D prior to washing. The precise amount of membrane inserted Dyngo-4a is difficult to measure as we discuss in the text. In order to make this clearer, we have now moved all these details to the discussion section where we elaborate on this. Furthermore, since Dyngo-4a, like cholesterol, is intercalating in between the head groups of the lipids the area would not increase in direct proportion to the mol%.

Also, there are no replicates shown, so unclear how reproducible these effects are?

Response: For clarity, only single experiments are shown. However, multiple experiments were performed and the range in measured values for 3 technical repeats can be observed in the standard deviations found in the main text (e.g., 6 ± 2 mol%).

The simulations are insufficiently described and difficult to interpret. How big are these systems? Why do the figures show the aqueous system with lateral boundaries?

Response: There are no explicit boundaries used in the simulations, periodic boundary conditions are applied in all three dimensions. The lateral boundaries observed in the figures correspond to the simulation box edges and are a visual artifact of 2D projections with QuickSurf representation. No artificial wall or constraints were introduced laterally. Additional technical details, including the system size and periodic boundary conditions have now been added to the methods section.

It seems quite important that multiple Dyngo molecules aggregate rather than partition into membranes - is this likely to occur in experiment?

Response: Yes, this is important and with the additional simulation experiments suggested by Reviewer #3 it has been clarified that they contribute a great deal to the change in lipid packing of lipid bilayers containing cholesterol. However, it is hard to test aggregation is the cellular system, but we believe that this happens and contribute to the effect on membranes. We have now emphasized the effect of the aggregates in the text.

PMF simulations are strongly suggesting that Dyngo does not spontaneously cross membranes, which is inconsistent with its drug-like amphiphilicity (cLogP~2.5 is optimally suited for membrane permeation) and known effects on intracellular proteins. This suggests an artefact in these PMFs.

Response:As stated in the submitted version of the manuscript, logP was used to validate the topology and the observed value was in a very good agreement with cLogP. Moreover, this validation complemented the standard procedure of CHARMM-GUI ligand modelling, that provided a reasonable penalty score (around 20) for the Dyngo-4a topology. POPC and cholesterol molecules are standard in the force field and validated by numerous studies. The parameters used for the membrane simulations and AWH in particular are very common for this type of studies. Thus, we do not see what may cause any artifacts in the free energy profile construction. In fact, amphiphilicity of the molecule may be one of the key reasons that Dyngo-4a molecule remains at the aqueous interface of the membrane and does not cross the membrane spontaneously. Also, we believe that the energy barrier of 40-60 kJ/mol is not prohibitively high and Dyngo-4a molecules may still overcome the barrier eventually, though we expect majority to reside in the upper leaflet*. *

The authors should experimentally measure the permeation of Dyngo through bilayers (or lack thereof), to more robustly support their finding that Dyngo does not cross membranes spontaneously.

-Response: We thank the reviewer for the suggestion, however this if very technically challenging and would require establishment of precise systems which is beyond the scope of this manuscript.

Why not measure effect of Dyngo on lipid packing directly and more broadly in model membranes?

-Response: With the added modelling experiments supporting the previous simulations and the calculated GP values from the C-Laurdan experiments on cellular plasma membrane, we do not find it necessary to include more model membranes experiments than the already existing ones on lipid monolayers and supported lipid bilayers.

Statistics should not be done on individual cells (n>26), but rather on independent experiment (N=3?)

-Response: We have performed the statistics on live cell particle tracking according to previous literature on similar systems (Boucrot et al., 2011; Larsson et al., 2023; Shvets et al., 2015; Stoeber et al., 2012).

Fig 1G is important but rather unclear. Firstly, these kymographs are an odd way to show that the caveolae are not moving. More importantly, caveolae in normal cells have been shown to be quite stable and immobile (eg doi: 10.1074/jbc.M117.791400), yet here they are claimed to be very mobile.

-Response: Although this might be an odd and unconventional way to depict dynamic processes, we believe that this is a very illustrative way to show track stability over time in bulk rather than just a kymograph over a few structures in a cell. Furthermore, we are not claiming that caveolae are very mobile but rather the opposite very stable in agreement with previous work (Boucrot et al., 2011; Larsson et al., 2023; Mohan et al., 2015). We have now edited the text to make this even clearer.

Also, if Dyngo prevents caveolae scission, there should be more of them at the membrane - why no quantification like Fig 1C to show accumulation of caveolae upon Dyngo treatment? Or directly counting caveolae via EM, as in Fig 4C?

-Response: We are currently preforming CTxB HRP experiments using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long. However, Dynasore has previously been shown, by EM, to increase the number of caveolae at the PM (Moren et al., 2012; Sinha et al., 2011).

The writing can be made more precise and referencing could be strengthened. Response: The introduction was written in a short format, and we have now extended this and made it more precise. Some examples: (a) 'scissoned' is not a word in English,

Response: Thanks, we have now changed this.

(b) what is meant by "Cav1 assembly is driven by high chol content"? There are many types of caveolin assemblies.

Response: We agree that this can be made more precise and have now clarified this in the introduction.

(c) "This generates a unique membrane domain with distinct lipid packing and a very high curvature." Unclear what 'this' refers to and there is no reference here, so what is the evidence for either of these claims? Caveolin-8S oligomers are not curved. Perhaps 'this' is caveolae, but they are relatively large and also not very highly curved and I am unaware of measurements of lipid packing therein.

Response: caveolae are around 50 nm which in biology is a very high curvature of a membrane. It has been extensively proven that caveolae have a distinct lipid composition highly enriched in cholesterol and sphingolipids, which thereby also will generate a unique lipid packing as compared to the surrounding membrane. Yet, the reviewer is correct that lipid packing has not been measured in a caveola for obvious technical challenges. Thus, we have now changed the text to “special lipid composition”.

The sentence following that one again makes a specific, but unreferenced, claim. (d) intro claims that lipid packing is critical for fission, but it is unclear quite what is meant by this claim. The references do not help, as they are often about the basic biophysics of lipids, rather than how packing affects fission.

Response: We have now edited the text.

(e) intro strongly implies that caveolae remain membrane attached because of stalled scission. How strong is the evidence for this? The fact that EHD2 is at the neck is not definitive,

Response: We used the term stalled scission to describe that all omega shaped membrane invaginations do not scission in the same automatic way as clathrin coated vesicles. We have now changed this in the text. Caveolae are shown to be released (undergo scission) and be detected as internal caveolae if the protein EHD2 is removed. Hence this must be interpreted as if EHD2 stalls scission. The evidence includes data compiled over the last 12 years from others and us which include for example: 1) Caveolae with EHD2 have a longer duration time (Larsson et al., 2023; Mohan et al., 2015; Moren et al., 2012; Stoeber et al., 2012), Knock down of EHD2 results in more internalized caveolae as measured by CTxB HRP using EM (Moren et al., 2012) and shorter duration time at the PM (Hubert et al., 2020; Larsson et al., 2023; Mohan et al., 2015; Stoeber et al., 2012). 2) EHD2 overexpression results in less internalized caveolae as measured by CTxB HRP using EM (Stoeber et al., 2012). Furthermore, 3) overexpression or acute addition of purified EHD2 via microinjection counteracts lipid induced scission of caveolae and hence result in caveolae stabilization at the PM (Hubert et al., 2020). It is very hard to see that the release and internalization of caveolae could result from anything else than that these have undergone scission. EHD2 has been found around the rim of caveolae (Matthaeus et al., 2022) and overexpression of EHD2 oligomerizing mutants have been shown to expand the caveola neck (Hoernke et al., 2017; Larsson et al., 2023).

(f) unclear what is meant by 'lipid packing frustration' and how Dyngo supposedly induces it.

Response: Lipid packing frustration refers to what is usually referred to as lipid packing defect, but since lipid membranes are describe as a fluid system it should not have defects whereby, we believe that lipid packing frustration is more accurate. However, we have now changed the text and use “decreased lipid packing” or “decreased lipid order” more thoroughly to describe the effect on the plasma membrane.

IF of Cav1 is insufficient to claim puncta as caveolae. Co-stained puncta of caveolin with cavin are much stronger evidence. Same issue for Cav1-GFP puncta.

Response: We agree and have now provided IF showing cavin1 and EHD2 colocalization to Cav1GFP in non and Dyngo-4a-treated cells.

Fig 3E claims that "preferred position of Dyngo-4a was closer to the head groups" but the minimum looks to be in similar place as Fig 3B without cholesterol.

Response:We appreciate the reviewer’s observation. The PMF minima in the POPC and POPC:Chol membranes are indeed close in absolute position (~1.1–1.2 nm from the bilayer center). However, as clarified in the revised text, the presence of cholesterol leads to a slight shift of Dyngo-4a closer to the headgroup region and broadens the positional distribution. This is also evident from the added density profiles (Fig. S3A) and is now described more precisely in the manuscript.

Critically, these results do not support the notion that Dyngo affects lipid packing sufficiently, which is not measured in the simulations (though could be).

-Response: We thank the reviewer for the excellent suggestion. In response, we have now included a detailed analysis of Dyngo-4a’s effect on lipid packing in the simulations. As described in the revised manuscript, we measured deuterium order parameters, area per lipid (APL), and lipid–Dyngo–cholesterol spatial distributions (Figs. 3-H, S3C-E). The results demonstrate that Dyngo-4a decreases lipid order in POPC:Chol membranes. Both single molecules and clusters reduce the order parameter by up to 0.04 units, particularly in the upper leaflet, where Dyngo-4a reside.The reduction is most pronounced in the midchain region of the sn1 tail and around the double bond of the sn2 tail. These effects were accompanied by increased APL in POPC:Chol membranes and by colocalization of Dyngo-4a near cholesterol-rich regions. Together, these data confirm that Dyngo-4a perturbs membrane organization and lipid packing in a composition-dependent manner. We believe these additions directly address the concern and demonstrate that the simulations indeed support the conclusion that Dyngo-4a modulates lipid packing.

Finally, the simulation data do not show "that Dyngo-4a is competing with cholesterol"; it is unclear what 'competition' means in this context, but regardless, the data only shows that Dyngo sits at a similar location as cholesterol.

We agree with the reviewer that “competition” was an imprecise term. We have rephrased the relevant sections to clarify that Dyngo-4a and cholesterol localize to overlapping regions and exhibit spatial coordination. As now stated in the manuscript, cholesterol appears to partially displace Dyngo-4a from its preferred depth seen in pure POPC, broadens its membrane distribution, and alters lipid packing. According to the order parameters there is an interplay between chol and Dyngo-4a and the heatmaps show that the distribution of chol in the membrane gets less uniform in the presence of Dyngo-4a. These interactions suggest that Dyngo-4a perturbs cholesterol-rich domains.

As new analysis routines were added to the study, we have now also added the details on those to the Methods section of the text.

AFM measures the stiffness of the cell (as correctly explained in Results section) not "overall stiffness of the PM" as stated in the Discussion.

Response: We thank the reviewer for pointing this out, we have now altered this in the discussion section.

Fig2A: what was the starting lipid surface pressure? How does Dyngo insertion depend on initial lipid packing?

Response: The starting pressure lipid pressure was 20 mN m-1 which we now have incorporated in the figure legend. We performed several such experiments with a starting pressure ranging from 20-23 mN m-1 showing consistent results which we described in the materials and methods section. Given that we also performed QCMD analysis and simulations on bilayers showing that Dyngo-4a adsorbed and inserted respectively, we have not performed a titration of starting pressures resulting in a MIP of Dygo-4a.

Fig 4B is a strange approach to measure membrane motion. Why not RMSD or some other displacement based method? As its shown, it implies that the area of the cell changes.

Response: The method that we used to quantify the area of the cell which is attached (or close to) the glass and thereby is visible in TIRF microscopy. This is area indeed changes over time which has been frequently observed and used to describe and quantify the mobility, lamellipodia and filopodia formation among other things. We agree that RMSD can also be used to analyze the data before and after treatments and we have now included RMSD­­­­ analysis in the manuscript.

Reviewer #3 (Significance (Required)):

The title, abstract, and introduction of the manuscript are largely framed around lipid packing, but most of the data investigate other unexpected effects of treating cells with Dyngo4a. The only measurement for lipid packing (or any other membrane properties) is Fig 4E-F. Therefore, this paper is effectively an investigation of an artefact of a common reagent, which itself could be a valuable contribution. However, the mechanism to explain its effect requires stronger evidence, and its broad biological significance needs further exploration.

Overall, the impact of documenting the effects of Dyngo4a on membranes appears modest but may be valuable to the membrane trafficking community.

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

Larsson et al present experimental and computational data on the role of Dyngo4a (a compound that was developed to inhibit dynamin) on the dynamics of caveolae. The manuscript mostly documents effects of Dyngo on caveolae, with one experiment to suggest a mechanism for this result. This one rather unconvincing result forms the focus of the manuscript contributing to a disconnect between the data and the presentation. Additionally, there are concerns with data interpretation. The writing could also benefit from revision to address grammar mistakes, strengthen referencing, and increase precision.

Overall, the manuscript requires substantial revisions before being considered for publication. The central claim, in particular, needs stronger evidence to support the proposed mechanism.

Significant issues (in approximate order of importance):

1. The data supporting the central mechanistic explanation appears limited. There is no evidence that Dyngo remains in one leaflet, the GP of the PM is very low compared to previous measurements, effects on other membranes are not explored, dynamin-directed effects of Dyngo are not considered,
2. The QCM-D measurements and claims require explanation as several aspects remains unclear. In Fig S2, the 'softness' (what does this mean?) changes by 4-fold with DMSO alone (what does this mean?), then fractionally more with Dyngo. Then fractionally more again when Dyngo is removed (why?). Then it remains somewhat higher when both Dyngo and DMSO are removed, which is somehow interpreted as Dyngo remaining in the bilayer, but not DMSO. These interpretations are difficult to grasp, as the authors seem to be implying simple amphiphilic partitioning into the membrane, which should all be removable by efficient washing. I do not doubt that this compound interacts with membranes, but the quantifications appear ambiguous. A bilayer with 16 mol% (or worse, 30% if all in one leaflet) Dyngo is very unlikely (to remain a bilayer). Even if such a bilayer was conceivable, the authors are claiming an ADDITION of Dyngo that would INCREASE the area of one leaflet by 30%, which needs explanation as it appears unlikely. Also, there are no replicates shown, so unclear how reproducible these effects are?
3. The simulations are insufficiently described and difficult to interpret. How big are these systems? Why do the figures show the aqueous system with lateral boundaries? It seems quite important that multiple Dyngo molecules aggregate rather than partition into membranes - is this likely to occur in experiment? PMF simulations are strongly suggesting that Dyngo does not spontaneously cross membranes, which is inconsistent with its drug-like amphiphilicity (cLogP~2.5 is optimally suited for membrane permeation) and known effects on intracellular proteins. This suggests an artefact in these PMFs. The authors should experimentally measure the permeation of Dyngo through bilayers (or lack thereof), to more robustly support their finding that Dyngo does not cross membranes spontaneously.
4. Why not measure effect of Dyngo on lipid packing directly and more broadly in model membranes?
5. Statistics should not be done on individual cells (n>26), but rather on independent experiment (N=3?)
6. Fig 1G is important but rather unclear. Firstly, these kymographs are an odd way to show that the caveolae are not moving. More importantly, caveolae in normal cells have been shown to be quite stable and immobile (eg doi: 10.1074/jbc.M117.791400), yet here they are claimed to be very mobile. Also, if Dyngo prevents caveolae scission, there should be more of them at the membrane - why no quantification like Fig 1C to show accumulation of caveolae upon Dyngo treatment? Or directly counting caveolae via EM, as in Fig 4C?
7. The writing can be made more precise and referencing could be strengthened. Some examples: (a) 'scissoned' is not a word in English, (b) what is meant by "Cav1 assembly is driven by high chol content"? There are many types of caveolin assemblies. (c) "This generates a unique membrane domain with distinct lipid packing and a very high curvature." Unclear what 'this' refers to and there is no reference here, so what is the evidence for either of these claims? Caveolin-8S oligomers are not curved. Perhaps 'this' is caveolae, but they are relatively large and also not very highly curved and I am unaware of measurements of lipid packing therein. The sentence following that one again makes a specific, but unreferenced, claim. (d) intro claims that lipid packing is critical for fission, but it is unclear quite what is meant by this claim. The references do not help, as they are often about the basic biophysics of lipids, rather than how packing affects fission. (e) intro strongly implies that caveolae remain membrane attached because of stalled scission. How strong is the evidence for this? The fact that EHD2 is at the neck is not definitive, (f) unclear what is meant by 'lipid packing frustration' and how Dyngo supposedly induces it.
8. IF of Cav1 is insufficient to claim puncta as caveolae. Co-stained puncta of caveolin with cavin are much stronger evidence. Same issue for Cav1-GFP puncta.
9. Fig 3E claims that "preferred position of Dyngo-4a was closer to the head groups" but the minimum looks to be in similar place as Fig 3B without cholesterol. Critically, these results do not support the notion that Dyngo affects lipid packing sufficiently, which is not measured in the simulations (though could be). Finally, the simulation data do not show "that Dyngo-4a is competing with cholesterol"; it is unclear what 'competition' means in this context, but regardless, the data only shows that Dyngo sits at a similar location as cholesterol.
10. AFM measures the stiffness of the cell (as correctly explained in Results section) not "overall stiffness of the PM" as stated in the Discussion.
11. Fig2A: what was the starting lipid surface pressure? How does Dyngo insertion depend on initial lipid packing?
12. Fig 4B is a strange approach to measure membrane motion. Why not RMSD or some other displacement based method? As its shown, it implies that the area of the cell changes.

Significance

The title, abstract, and introduction of the manuscript are largely framed around lipid packing, but most of the data investigate other unexpected effects of treating cells with Dyngo4a. The only measurement for lipid packing (or any other membrane properties) is Fig 4E-F. Therefore, this paper is effectively an investigation of an artefact of a common reagent, which itself could be a valuable contribution. However, the mechanism to explain its effect requires stronger evidence, and its broad biological significance needs further exploration.

Overall, the impact of documenting the effects of Dyngo4a on membranes appears modest but may be valuable to the membrane trafficking community.

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

This manuscript uses the small molecule dynamin inhibitors dynasore and dyngo to show that in dynamin triple knockout cells that these inhibitors impact lipid packing and organization in the plasma membrane. Data showing that dyngo affects caveolin dynamics using tirf microscopy is also shown and is interpreted to reflect inhibition of caveolae scission from the membrane.

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane. What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane. Study of caveolae endocytosis is based on a TIRF assay that has inherent limitations:

• Caveolae are defined as bright cav1-positive spots in diffraction limited TIRF and their disappearance presumed to be endocytic events. Cav1 spots are presumed to be caveolae but the authors do not consider that they may be flat non-caveolar oligomers. The diffraction limited TIRF approach interprets the large structures as caveolae but evidence to that effect is lacking.
• The analysis (and the diagram presented in figure 4) considers that caveolae can either diffuse laterally in the membrane or internalize and does not consider that caveolae can flatten and possibly fragment in the membrane. Is it not possible that loss of Cav1 spots is a fragmentation event and not necessarily a scission event?
• The analysis is based on overexpression of Cav1-GFP that may alter the stoichiometry between Cav1 and cavin1 such that while caveolae may be expressed, larger non-caveolar structures may accumulate.
• Cav1 has been shown to be internalized via the CLIC pathway (Chaudary et al, 2014) and if dyngo is impacting clathrin then maybe it is also impacting CLIC endocytosis and thereby Cav1 endocytosis via this pathway?
• The longer Cav1 TIRF track time and shorter displacement with dyngo is consistent with inhibition of caveolae scission. However, as the authors discuss, could not reduced membrane undulations due to dyngo's impact on membrane order be responsible for the longer tracks? Alternatively, perhaps the altered lipid packing is corralling Cav1 movement and reducing non-caveolar Cav1 endocytosis, resulting in shorter tracks of longer duration? The proposed interaction of dyngo with cholesterol could prevent scission but also stabilize large (flat?) Cav1 oligomers in the membrane, perhaps reducing Cav1 oligomer fragmentation.

My point here is not to discredit the data but only to suggest that the TIRF approach used is an indirect measure of caveolae scission from the membrane that requires substantiation using other approaches.

Dyngo is certainly generally affecting lipid packing via cholesterol and thereby affecting Cav1 dynamics in the plasma membrane. The claim of caveolae scission should be qualified and alternative possibilities considered and discussed. If the authors persist in arguing that dyngo is affecting caveolae scission then the effect should be substantiated by accumulation of caveolae by quantitative EM and high spatial and temporal resolution imaging of Cav1 and cavin1 to define the endocytic events. As the latter represents a new, and potentially very challenging, line of experimentation, I would suggest that it is beyond the scope of the current study. As indicated above the additional experiments are not necessary and qualification of the claims would be sufficient.

Other points

Figure 1C - Cav1 positive spots cannot be interpreted to be caveolae from diffraction limited confocal images. Same comment applies to Fig 4G - caveola? duration.

Figure 4C - it is not clear why this EM data is not quantified - for both the number of caveolae and clathrin coated pits - as this would help clarify the interpretation of the effect reported.

Figure 4D - the AFM experiments should perhaps be repeated as the non-significant effect of dyngo on the Young's modulus may be a result of insufficient n values.

Significance

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane.

What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane.

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Referee #1

Evidence, reproducibility and clarity

The authors use Dyngo-4a, a known Dynami inhibitor to test its influence on caveolar assembly and surface mobility. They investigate, whether it incorporates into membranes with Quartz-Crystal Microbalance, they investigate how it is organized in membranes using simulations. Finally, they use lipid-packing sensitive dyes to investigate lipid packing in the presence of Dyngo-4a, membrane stiffness using AFM and membrane undulation using fluorescence microscopy. They also use a measure they call "caveola duration time" to claim that something happens to caveolae after Dyngo-4a addition and using this parameter, they do indeed see an increase in it in response to Dyngo-4a, which is reduced back to the baseline after addition of cholesterol.

Overall, the authors claim: 1) Dyngo-4a inserts into the membrane and this 2) results in "a dramatic dynamin-independent inhibition of caveola scission". 3) Dyngo-4a was inserted and positioned at the level of cholesterol in the bilayer and 4) Dyngo-4a-treatment resulted in decreased lipid packing in the outer leaflet of the plasma membrane 5) but Dyngo-4a did not affect caveola morphology, caveolae- associated proteins, or the overall membrane stiffness 6) acute addition of cholesterol counteracts the block in caveola scission caused by Dyngo-4a

Overall, in this reviewers opinion, claims 1, 3, 4, 5 are well-supported by the presented data from electron and live cell microscopy, QCM-D and AFM. However, there is no convincing assay for caveolar endocytosis presented besides the "caveola duration" which although unclearly described seems to be the time it takes in imaging until a caveolae is not picked up by the tracking software anymore in TIRF microscopy. Since the main claim of the paper is a mechanism of caveolar endocytosis being blocked by Dyngo-4a, a true caveolar internalization assays is required to make this claim. This means either the intracellular detection of not surface connected caveolar cargo or the quantification of caveolar movement from TIRF into epifluorescence detection in the fluorescence microscope. Otherwise, the authors could remove the claim and just claim that caveolar mobility is influenced.

Significance

A number of small molecule inhibitors for the GTPase dynamics exist, that are commonly used tools in the investigation of endocytosis. This goes as far that the use of some of these inhibitors alone is considered in some publications as sufficient to declare a process to be dynamin-dependent. However, this is not correct, as there are considerable off-target effects, including the inhibition of caveolar internalization by a dynamin-independent mechanism. This is important, as for example the influence of dynamin small molecule inhibitors on chemotherapy resistance is currently investigated (see for example Tremblay et al., Nature Communications, 2020).

The investigation of the true effect of small molecules discovered as and used as specific inhibitors and their offside effects is extremely important and this reviewer applauds the effort. It is important that inhibitors are not used alone, but other means of targeting a mechanism are exploited as well in functional studies. The audience here thus is besides membrane biophysicists interested in the immediate effect of the small molecule Dyngo-4a also cell biologists and everyone using dynamic inhibitors to investigate cellular function.

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Reply to the reviewers

Reviewer #1 (Evidence, Reproducibility, and Clarity)

Reviewer comment: This is a very well conceived study of responses to plasma membrane stresses in yeast that signal through the conserved TORC2 complex. Physical stress through small molecular intercalators in the plasma membrane is shown to be independent of their biochemistry and then studies for its effect on plasma membrane morphology and the distribution of free ergosterol (the yeast equivalent of cholesterol), with free being the pool of cholesterol that is available to probes and/or sterol transfer proteins. Experiments nicely demonstrate a negative feedback loop consisting of: stress -> increased free sterol and TORC2 inhibition -> activation of LAM proteins (as demonstrated by Relents and co-workers previously) -> removal of free sterol -> return to unstressed state of PM and TORC2.

Author response: We thank the reviewer for their positive and encouraging feedback. We are pleased to submit our revised manuscript and have addressed all points raised below.

Comment: Fig 2A: Is detection of PIP/PIP2/PS linear for target, or possibly just showing availability that is increased due to local positive curvature?

Response: This is an excellent and fundamental question. While FLARE signal likely reflects lipid availability, its detection is indeed influenced by factors such as membrane curvature and lipid composition, due to varying insertion depths of the lipid-binding domains. For example, studies using NMR suggest that the PLCδ PH domain partially inserts into membranes, potentially conferring curvature sensitivity (Flesch et al., 2005; Uekama et al., 2009). Similarly, curvature influences lactadherin binding, though it's unclear if this extends to its isolated C2 domain (Otzen et al., 2012; Shao et al., 2008; Shi et al., 2004). We could not find direct evidence for curvature sensitivity of P4C(SidC), but assume some influence exists.

To avoid overinterpreting these limitations, we now describe our data based solely on the FLAREs used, rather than inferring enrichment of specific lipid species. We refer to these PM structures as "PI(4,5)P₂-containing", consistent with prior literature (Riggi et al., 2018) and have revised our manuscript accordingly.

Comment: Can any marker be identified for the D4H spots at 2 minutes? In particular, are they early endosomes (shown by brief pre-incubation with FM4-64)?

Response: We appreciate the reviewer's suggestion and have now added new data (Fig. S2E-H). We tested colocalization of D4H spots with FM4-64 (early endosomes), GFP-VPS21 (early endosome marker), and LipidSpot{trade mark, serif} 488 (lipid droplets), but found no overlap. This later observation was not unexpected given that D4H does not recognize Sterol esters. D4H foci also did not overlap with ER (dsRED-HDEL), though they were frequently adjacent to it. While their exact identity remains unknown, we agree this is an intriguing direction for future investigation.

Comment: Is there any functional (& direct) link between Arp inhibition (as in the Pombe study of LAMs by the lab of Sophie Martin) and PM disturbance by amphipathic molecules?

Response: We have explored this connection and now present new data (see final paragraph of Results). Briefly, we show that CK-666 induces internalization of PM sterols in a Lam2/4-dependent manner, and that TORC2 activity is more strongly reduced in lam2Δ lam4Δ cells compared to WT. These findings support the idea that, like PalmC, Arp2/3 inhibition triggers a PM stress that is counteracted by sterol internalization.

Minor Comment: Fig 2A: Labels not clear. Say for each part what FP is used for pip2.

Response: As noted above, we revised image labels to clarify which FLAREs were used, and refer to data accordingly throughout.

Minor Comment: Move fig s2d to main ms. The 1 min and 2 min data are integral to the story.

Response: We agree and have incorporated the 1-min and 2-min data into the main figures. Vehicle-treated controls were moved to Fig. S2.

Minor Comment: The role of Lam2 and Lam4 in retrograde sterol transport has in vivo only been linked to one of their two StART domains not both, as mentioned in the text.

Response: Thank you for pointing this out. We have corrected the text to:

"[...]Lam2 and Lam4[...] contain two START domains, of which at least one has been demonstrated to facilitate sterol transport between membranes (Gatta et al., 2015; Jentsch et al., 2018; Tong et al., 2018)."

Minor Comment: Throughout, images of tagged D4H should be labelled as such, not as "Ergosterol".

Response: We have updated all relevant figure labels and text to refer to "D4H" rather than "Ergosterol", in line with this recommendation.

Reviewer #1 (Significance):

These results in budding yeast are likely to be directly applicable to a wide range of eukaryotic cells, if not all of them. I expect this paper to be a significant guide of research in this area. The paper specifically points out that the current experiments do not distinguish the precise causation among the two outcomes of stress: increased free sterol and TORC2 inhibition. Of these two outcomes which causes which is not yet known. If data were added that shed light on this causation that would make this work much more signifiant, but I can understand 100% that this extra step lies beyond - for a later study for which the current one forms the bedrock.

Response:

We thank the reviewer for their generous assessment. We agree that understanding the causality between increased free sterol and TORC2 inhibition is a critical next step.

Based on our current data, we believe the increase in free ergosterol precedes TORC2 inhibition. For example, TORC2 inhibition alone (e.g., via pharmacological means) does not initially increase free sterol, while it does enhance Lam2/4 activity, promoting sterol internalization (Fig. 3A). Baseline TORC2 activity also inversely correlates with free PM sterol levels in lam2Δ lam4Δ versus LAM2T518A LAM4S401A cells (Figs. 2D, S2C).

Additionally, during sterol depletion, we observe an initial increase in TORC2 activity before growth inhibition occurs, after which activity declines-likely due to compromised PM integrity (Fig. S2M). We now also show that adaptation to several other stresses (e.g., osmotic shock, heat shock, CK-666) partially depends on sterol internalization, which correlates with TORC2 activation (Fig. 4, S4B).

While these findings strengthen the model that PM stress perturbs sterol availability and secondarily impacts TORC2, we cannot yet definitively demonstrate causality. As suggested by Reviewer 3, we tested cholesterol-producing yeast (Souza et al., 2011), but found their response to PalmC indistinguishable from WT, making it difficult to draw mechanistic conclusions (Rebuttal Fig. 2).

Taken together, we favour a model where sterols affect PM properties sensed by TORC2, probably lipid-packing, rather than acting as direct effectors. We hope our revised manuscript more clearly conveys this model and serves as a strong foundation for future mechanistic studies.

Reviewer #2 (Evidence, Reproducibility, and Clarity)

Reviewer comment: This manuscript describes multiple effects of positively-charged membrane-intercalating amphipaths (palmitoylcarnitine, PalmC, in particular) on TORC2 in yeast plasma membranes. It is a "next step" in the Loewith laboratory's characterization of the effect of this agent on this system. The study confirms the findings of Riggi et al.(2018) that PalmC inhibits TORC2 and drives the formation of membrane invaginations that contain phosphatidylinositol-bis-phosphate (PIP2) and other anionic phospholipids. It also demonstrates that PalmC intercalates into the membrane, acts directly (rather than through secondary metabolism) and is representative of a class of cationic amphipaths. The interesting finding here is that PalmC causes a rapid initial increase in the plasma membrane ergosterol accessible to the DH4 sterol probe followed by a decrease caused by its transfer to the cytoplasm through its transporter, LAM2/4. TORC2 is implicated in these processes. Loewith et al. have pioneered in this area and this study clearly shows their expertise. Several of the findings reported here are novel. However, I am concerned that PalmC may not be revealing the physiology of the system but rather adding tangential complexity. (This concern applies to the precursor studies using PalmC to probe the TORC2 system.) In particular, I am not confident that the data justify the authors' conclusions "...that TORC2 acts in a feedback loop to control active sterol levels at the PM and [the results] introduce sterols as possible TORC2 signalling modulators."

Author response:

We thank Reviewer #2 for the constructive and critical evaluation of our work. We appreciate the acknowledgment of the novelty and technical strength of several of our findings, and we understand the concern that PalmC could be eliciting non-physiological effects. Our study was designed precisely to use PalmC and similar membrane-active amphipaths as tools to strongly perturb the plasma membrane (PM) in a controlled and tractable way. We now state this intention explicitly in both the Introduction and Discussion sections. To address concerns about the specificity and physiological relevance of PalmC, we have expanded our dataset to include additional PM stressors (hyperosmotic shock, Arp2/3 inhibition, and heat shock), all of which reproduce key features observed with PalmC-namely, TORC2 inhibition, PM invaginations, and retrograde sterol transport (Fig. 4, S4).

We hope this more comprehensive dataset, along with revised discussion and clarified claims, addresses the reviewer's concerns regarding physiological interpretation and artifact.

Major issues 1 and 2: 1. The invaginations induced by PalmC may not be physiologic but simply the result of the well-known "bilayer couple" bending of the bilayer due to the accumulation of cationic amphipaths in the inner leaflet of the plasma membrane bilayer which is rich in anionic phospholipids. Such unphysiological effects make the observed correlation of invagination with TORC2 inhibition etc. hard to interpret.

Electrostatic/hydrophobic association of PIP2 with PalmC could sequester the anionic phospholipid(s). Such associations could also drive the accumulation of PIP2 in the invaginations. This could explain PalmC inhibition of TORC2 through a simple physical rather than biological process. So, it is difficult to draw any physiological conclusion about PIP2 from these experiments.

Response to major issues 1 and 2:

We agree that amphipath-induced bilayer stress, including via the bilayer-couple mechanism, may contribute to PM curvature changes. However, the reviewer's assumption that PalmC inserts preferentially into the inner leaflet appears inconsistent with both literature and our observations. PalmC is zwitterionic, not cationic, and is unlikely to electrostatically sequester anionic lipids such as PIP2. For clarification, we included a short summary of our proposed mechanism of PalmC in the context of the current literature in our Discussion:

"[...] study it was also demonstrated that addition of phospholipids to the outer PM leaflet causes an excess of free sterol at the inner PM leaflet, and its subsequent retrograde transport to lipid droplets (Doktorova et al., 2025). Although we cannot exclude that it is the substrate of a flippase or scramblase, PalmC is not a metabolite found in yeast, nor, given its charged headgroup, is it likely to spontaneously flip to the inner leaflet (Goñi, Requero and Alonso, 1996). Thus, we propose that PalmC accumulates in the outer leaflet, disrupts the lipid balance with the inner leaflet which is, similarly to the mammalian cell model (Doktorova et al., 2025), rectified by sterol mobilization, flipping and internalization (Fig. 5B)."

While we agree that PM invaginations per se are not the central focus of this study, they are indeed a reproducible and biologically intriguing phenomenon. We emphasize that similar invaginations occur not only during PalmC treatment but also in response to other physiological stresses, such as hyperosmotic shock and Arp2/3 inhibition (Fig. 4), and have been reported independently by others (Phan et al., 2025). Furthermore, related structures have been documented in yeast mutants with altered PIP2 metabolism or TORC2 hyperactivity (Rodríguez-Escudero et al., 2018; Sakata et al., 2022; Stefan et al., 2002), and even in mammalian neurons with SJ1 phosphatase mutations (Stefan et al., 2002). These observations support our interpretation that the observed invaginations represent an exaggerated manifestation of a physiologically relevant stress-adaptive process. In our previous study we indeed proposed that PI(4,5)P2 enrichment in PM invaginations was important for PalmC-induced TORC2 inactivation, using the heat sensitive PI(4,5)P2 kinase allele mss4ts - a rather blunt tool (Riggi et al., 2018). We have now come to the conclusion that different mechanisms other than, or in addition to, PIP2 changes drive TORC2 inhibition in our system. In this study, we use the 2xPH(PLC) FLARE exclusively as a generic PM marker, not as a readout of PIP2 biology. Rather, we propose that sterol redistribution and/or the biophysical impact that this has on the PM are central drivers, with TORC2 acting as a signaling node that senses and adjusts PM composition accordingly.

We now clarify these arguments in the revised Discussion and have reframed our use of PalmC as a probe to explore the capacity of the PM to adapt to acute stress via dynamic lipid rearrangements.

Major issue 3:

As the authors point out, a large number of intercalated amphipaths displace sterols from their association with bilayer phospholipids. This unphysiologic mechanism can explain how PalmC causes the transient increase in the availability of plasma membrane ergosterol to the D4H probe and its subsequent removal from the plasma membrane via LAM2/4. TORC2 regulation may not be involved. In fact, the authors say that "TORC2 inhibition, and thereby Lam2/4 activation, cannot be the only trigger for PalmC induced sterol removal." Furthermore, the subsequent recovery of plasma membrane ergosterol could simply reflect homeostatic responses independent of the components studied here.

Response:

We agree that increased free sterols in the inner leaflet likely initiate retrograde transport. Our results suggest that TORC2 inhibition facilitates this process by disinhibiting Lam2/4, allowing more efficient clearance of ergosterol from the PM (Fig. 3A, S2C). However, the process is not exclusively dependent on TORC2, and we state this explicitly.

We do not observe recovery of PM ergosterol on the timescales measured, while TORC2 activity recovers, suggesting that restoration likely occurs later via biosynthetic or anterograde trafficking pathways, which are outside the scope of this study. These points are clarified in the revised Discussion.

Major issue 3a:

The data suggest that LAM2/4 mediates the return of cytoplasmic ergosterol to the plasma membrane. To my knowledge, this is a nice finding that not been reported previously and is worth confirming more directly.

Response:

We thank the reviewer for this observation but would like to clarify a misunderstanding: our data do not suggest that Lam2/4 mediates anterograde sterol transport. Our results and prior work (Gatta et al., 2015; Roelants et al., 2018) show that Lam2/4 mediate retrograde transport from the PM to the ER, and TORC2 inhibits this process. We now clarify this point in the revised manuscript, stating:

"In vivo, Lam2/4 seem to predominantly transport sterols from the PM to the ER, following the concentration gradient (Gatta et al., 2015; Jentsch et al., 2018; Tong et al., 2018)."

Major issue 4:

I agree with the authors that "It is unclear if the excess of free sterols itself is part of the inhibitory signal to TORC2..." Instead, the inhibition of TORC2 by PalmC may simply result from its artifactual aggregation of the anionic phospholipids (especially, PIP2) needed for TORC2 activity. This would not be biologically meaningful. If the authors wish to show that accessible ergosterol inhibits TORC2 activity or vice versa, they should use more direct methods. For example, neutral amphipaths that do not cause the aforementioned PalmC perturbations should still increase plasma membrane ergosterol and send it through LAM2/4 to the ER.

Response:

We now provide evidence that three orthologous treatments (hyperosmotic shock, heat shock and Arp2/3 inhibition) similarly cause sterol mobilization and, in the absence of sterol clearance from the PM, prolonged TORC2 inhibition. These results do not support the reviewer's contention that the inhibition of TORC2 by PalmC is simply resulting from its artifactual aggregation of the anionic phospholipids. Furthermore, PalmC is zwitterionic, and its interaction with anionic lipids should be somewhat limited.

In our experimental setup, neutral amphipaths did not trigger TORC2 inhibition or D4H redistribution While this differs from prior in vitro work (Lange et al., 2009), we attribute this in part to a discrepancy to experimental setup differences, including flow chamber artifacts that we discuss in the methods section.

Importantly, only amphipaths with a charged headgroup, including zwitterionic (PalmC) and positively charged analogs, produced robust effects. A negatively charged derivative also seemed to have a minor effect on TORC2 activity and PM sterol internalization (Palmitoylglycine (Fig. 1D, Rebuttal Fig. 1). This suggests that in vivo, charge-based membrane perturbation is required to alter PM sterol distribution and TORC2 activity.

Major issue 5.:

The mechanistic relationship between TORC2 activity and ergosterol suggested in the title, abstract, and discussion is not secure. I agree with the concluding section of the manuscript called "Limitations of the study". It highlights the need for a better approach to the interplay between TORC2 and ergosterol.

Response:

This may have been true of the previous submission, but we now demonstrate that provoking PM stress in four orthogonal ways triggers mobilization of sterols, which left uncleared, prevents normal (re)activation of TORC2 activity. We thus conclude that free sterols, directly or more likely indirectly, inhibit TORC2. The role that TORC2 plays in sterol retrotranslocation has been demonstrated previously (Roelants et al., 2018). We believe our expanded data and clarified framework make a compelling case for a stress-adaptive role of sterol retrograde transport that is supervised and modulated-but not fully driven-by TORC2 activity.

Thus, we feel in the present version of this manuscript that the title is now justified.

Minor issue: Based on earlier work using the reporter fliptR, the authors claim that PalmC reduces membrane tension. They should consider that this intercalated dye senses many variables including membrane tension but also lipid packing. I suspect that, by intercalating into and thereby altering the bilayer, PalmC is affecting the latter rather than the former.

Response:

We thank the reviewer for this important point regarding the multifactorial sensitivity of intercalating dyes such as Flipper-TR®, including to membrane tension and lipid packing.

We respectfully note, however, that our current study does not include any new data generated using Flipper-TR®. We referred to earlier work (Riggi et al., 2018) for context, where Flipper-TR® was used as a membrane tension reporter.

We fully agree that the response of such "smart" membrane probes integrates multiple biophysical parameters-including tension, packing, and hydration-which are themselves interrelated as consequences of membrane composition (Colom et al., 2018; Ragaller et al., 2024; Torra et al., 2024). Indeed, this interconnectedness is central to our interpretation of PalmC's pleiotropic effects on the plasma membrane (PM). In our previous study, we observed that PalmC treatment not only reduced apparent PM tension (as measured by Flipper-TR®) but also increased membrane order ((Riggi et al., 2018); see laurdan GP, Fig. 6C), and here we show that it promotes the redistribution of free sterol away from the PM.

Furthermore, PalmC's effect on membrane tension was supported by orthogonal in vitro data: its addition to giant unilamellar vesicles (GUVs) led to a measurable increase in membrane surface area and decreased tension, as shown by pipette aspiration ((Riggi et al., 2018), Fig. 3F). This provides complementary evidence that the membrane tension reduction is not merely an artifact of Flipper-TR® reporting.

That said, we agree with the reviewer that in the case of TORC2 inhibition or hyperactivation, the observed changes in PM tension are based solely on Flipper-TR® data, without additional orthogonal validation. To address this concern, we have revised the relevant text in the manuscript to more cautiously reflect this complexity. The revised sentence now reads:

"Consistent with this role, data generated with the lipid packing reporter dye Flipper-TR® suggest that acute chemical inhibition of TORC2 increases PM tension, while Ypk1 hyperactivation decreases it."

This revised phrasing acknowledges both the utility and the limitations of Flipper-TR® as a probe of membrane biophysics.

Reviewer #2 Significance:

This is an interesting topic. However, use of the exogenous probe, palmitoylcarnitine, could be causing multiple changes that complicate the interpretation of the data.

Reviewers #1 and #3 were much more impressed by this study than I was. I am not a yeast expert and so I may have missed or confused something. I would therefore welcome their expert feedback regarding my comments (#2). Ted Steck

Response:

Thank you for your constructive feedback.

We believe that the manuscript is now much improved, and we hope to have convinced you that the mechanisms that we've elucidated using PalmC represent a general adaptation response to physiological PM stressors.

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

Reviewer comment: The authors describe the effects of surfactant-like molecules on the plasma membrane (PM) and its associated TORC2 complex. Addition of the surfactants with a positively-charged headgroup and a hydro-carbon tail of at least 16 caused the rapid clustering of PI-4,5P2 together with PI-4P and phosphatidylserine in large membrane invaginations. The authors convincingly demonstrate that this effect of the surfactants on the PM is likely caused by a direct disturbance of the PM organization and/or lipid composition. Interestingly, upon PalmC treatment, free ergosterol of the PM was found to first concentrate in the clusters, but within The kinetics of the changes in free ergosterol levels and the changes in TORC2 activity do not match. Ergosterol is rapidly depleted after PalmC treatment (The Lam2/4 data support the idea that ergosterol transport plays a role in the TORC2 recovery, but what role this is, is not clear to me. I think the data fit better with a model in which PalmC causes low tension of the PM which in turn disrupts normal lipid organization and thus causes TORC2 to shut down, maybe not by changes in free ergosterol but by changes, for instance, in lipid raft formation (which is in part effected by ergosterol levels). The transport of ergosterol is only one mechanism that is involved in restoring PM tension and TORC2 activity. However, sensing free ergosterol alone is most likely not the mechanism explaining how TORC2 senses PM tension.

Therefore, I recommend that the model is revised (or supported by more data), reflecting the fact that free ergosterol levels do not directly correlate with the TORC2 activity, but instead might be only one of the PM parameters that regulate TORC2.

Author response:

We thank the reviewer for their thoughtful assessment and constructive suggestions. As described in more detail above, we have included in our revised version of this manuscript a variety of new data, including the sterol-internalization dependent adaptation of the PM and regulation of TORC2 during additional stresses. We think that these data vastly improve on our previous manuscript version. We have addressed each point risen by the reviewer below and revised the manuscript accordingly, including a rewritten discussion and updated model to better reflect the limitations of our current understanding of how TORC2 senses changes in the plasma membrane (PM). It is true that the appearance of PM invaginations tracks well with TORC2 inhibition, but it is not clear to us if they are upstream of this inhibition or merely another symptom of the preceding PM perturbation (PalmC-induced free sterol increase can be observed after 10s (Fig. S2A), but PM invaginations become visible only after ~1 min - meanwhile we can observe near complete TORC2 inhibition after 30s). In this study, we are mostly interested in the role of PM sterol redistribution in stress response. Indeed we think that the role of free sterol clearance during stresses is to adapt the PM to these stresses - thus restoring PM parameters which in turn reactivates TORC2. This can be seen for hyperosmotic stress and the newly introduced PM stressors, Arp2/3 inhibition and heat shock response (Fig. 4). We have therefore softened our model and updated discussion and final figure (Fig. 5) to reflect that TORC2 likely responds to broader changes in PM organization or tension, with sterol redistribution representing one of several contributing factors rather than the sole signal.

Comment: - If TORC2 is indeed inhibited by free ergosterol, the addition of ergosterol to the growth medium should be able to trigger similar effects as PalmC. If this detection of free ergosterol is very specific (e.g. if TORC2 has a binding pocket for ergosterol) we would expect that addition of other sterols such a cholesterol or ergosterol precursors should not inhibit TORC2.

Response:

We appreciate this suggestion and agree that testing whether exogenous ergosterol can mimic PalmC effects would help assess specificity. However, yeast do not readily take up sterols under aerobic conditions, which renders artificial sterol enrichment at the yeast PM rather difficult. We have now included additional data characterizing our Lam2/4 mutants (see below), and pharmacological sterol synthesis inhibition, showing that a depletion of free sterols from the PM correlates with lower TORC2 activity (Fig. 2D, S2C). Additionally, as suggested, we tried to probe if ergosterol directly interacts with TORC2 through a specific binding pocket, by treating a yeast strain expressing cholesterol rather than ergosterol (Souza et al., 2011) with PalmC. However, the response of TORC2 activity in these cells was very similar to that of WT cells (Rebuttal Fig. 2). In conclusion, we agree that at present we do not know mechanistically how sterols affect TORC2 activity, although it does indeed seem more likely to be through an indirect mechanism linked to changes in PM parameters. The nature of such a mechanism will be subject to further studies. We hope that the introduced changes to the manuscript adequately reflect these considerations.

Rebuttal Fig. 2: WT yeast cells which produce ergosterol as main sterol, and mutant cells which produce cholesterol instead were treated with 5 µM PalmC, and TORC2 activity was assessed by relative phosphorylation of Ypk1 on WB. One representative experiment out of two replicates.

Comment: - The experiment in Figure 1C is not controlled for differences in membrane intercalation of the different compounds. For instance, does C16 choline and C16 glycine accumulate at the same rate in the PM (measure similar to experiment in Figure 1B). Maybe the positive charge at the headgroup of the surfactants increases the local concentration at the PM and therefore can explain the difference in effect on the PM.

Response:

We agree with the reviewer that the effects of the various PalmC derivatives are not directly controlled for differences in membrane intercalation. Our structure-activity screen was intended to demonstrate the general biophysical mode of action of PalmC-like compounds and to define minimal structural requirements for activity.

We now note in the manuscript that differential membrane insertion could contribute to the observed variation in efficacy, particularly in relation to tail length. While we considered this additional suggested experiment, it was ultimately judged to be outside the scope of this study due to its complexity and limited impact on the central conclusions.

A clarifying sentence has been added to the relevant results section to explicitly acknowledge this limitation:

"We did not control for differences in PM intercalation efficiency."

We also include a discussion here to further clarify our interpretation. Prior in vitro studies have shown that while intercalation is necessary, it is not sufficient for PM perturbation. For example, palmitoyl-CoA intercalates into membranes but does not induce the same biophysical effects as PalmC (Goñi et al., 1996; Ho et al., 2002). Thus, we believe that intercalation is only part of the story, and that the intrinsic propensity of different headgroups to perturb the PM plays a key role in the disruption of PM lipid organization.

Comment: - Are the intracellular ergosterol structures associated (or in close proximity) with lipid droplets (ergosterol being modified and delivered into a lipid droplet)?

Response:

We thank the reviewer for raising this point. We now include additional data (Fig. S2H) showing that intracellular D4H-positive structures do not reside near or colocalize with lipid droplets. The latter is not entirely unexpected as D4H does not recognize esterified sterols. However, we do observe an increase in overall LD volume following PalmC treatment, consistent with the idea that internalized PM sterols may be stored in LDs as sterol esters over time - although we did not test if this increase in LD volume is Lam2/4 dependent. This increase is mentioned in the revised results text. An increase in cellular LDs has also been recently reported during hyperosmotic shock (Phan et al., 2025).

For more attempts to identify a marker for intracellular D4H foci, see reply to reviewer 1.

Comment:

• How does the AA and DD mutations in Lam2/4 change the localization of the ergosterol sensor (before and after PalmC treatment).

Response:

We thank the reviewer for this question, as in the course of generating these data we realized that our "inhibited" DD mutant was in fact not phosphomimetic but displayed the same D4H distribution as the "hyperactive" AA mutant, i.e. a marked inwards shift of D4H signal away from the PM to internal structures due to increased PM-ER retrograde transport of sterols (Fig. S2C). This led us to critically re-evaluate and ultimately repeat our TORC2 activity WB experiments for PalmC treatment in LAM2/4 mutants. In this new set of experiments, the faster TORC2 recovery after PalmC treatment in the LAM2T518A LAM4S401A mutant did unfortunately not repeat robustly. It is possible that such differences can be observed under specific conditions. Nevertheless, the improved overall quality of the Western blot data allowed us to make the observation that baseline activity was already slightly different in these strains. The Lam2/4 centered part of the results section has subsequently been updated in the manuscript:

"Using a phosphospecific antibody, we did not observe an increase in baseline TORC2 activity in lam2Δ lam4Δ cells, which had been previously reported by electrophoretic mobility shift (Murley et al., 2017). Instead, baseline TORC2 activity was consistently slightly decreased in these cells (Fig. 2D). Ypk1, activated directly by TORC2, inhibits Lam2 and Lam4 through phosphorylation on Thr518 and Ser401, respectively (Roelants et al., 2018; Topolska et al., 2020). We substituted these residues with alanine, generating a strain in which Lam2/4 were no longer inhibited by phosphorylation (Roelants et al., 2018). In these cells, yeGFP-D4H showed that free sterols were constitutively shifted away from the PM to intracellular structures (Fig. S2C, bottom panel). Intriguingly, in opposition to lam2Δ lam4Δ cells, basal TORC2 activity was increased in LAM2T518A LAM4S401A cells (Fig. 2D). This suggests that a decrease in free PM sterols stimulates TORC2 activity [...]"

"In LAM2T518A LAM4S401A cells, TORC2 activity recovers with similar kinetics as the WT (Fig. 2D, bottom blot), suggesting that Lam2/4 release from TORC2 dependent inhibition during PalmC treatment is a fast and efficient process in WT cells, not further expedited by these constitutively active Lams."

As suggested, we also observed D4H localization in LAM2T518A LAM4S401A after PalmC treatment, and implemented these data to further demonstrate that PalmC causes an increase in the fraction of free ergosterol at the PM, which is subsequently removed:

"PalmC addition to LAM2T518A LAM4S401A cells likewise resulted first in a transient increase and then a further decrease in PM yeGFP-D4H signal (Fig. 3C, S3D)."

Comment: - Does Lam2/4 localize to ER-PM contact sites near the large PM invaginations, which could allow for efficient transport of the free ergosterol that accumulates in these structures.

Response:

We were curious about this too, and have now added the requested data in our supplementary material and added a sentence in our results:

"Indeed, in cells expressing GFP-Lam2 we observed that PalmC induced PM invaginations often formed at sites with preexisting GFP-Lam2 foci (Fig. S2K, cyan arrow), although GFP-Lam2 foci did not always colocalize with invaginations (Fig. S2K, yellow arrow) and vice versa. "

Additionally, in the effort to characterize intracellular D4H foci during PalmC as requested by reviewer 1, we also looked at the localization of these foci relative to ER, and found that

"During early timepoints, intracellular foci are usually in close vicinity to ER (Fig. S2E)"

Reviewer #3 (Significance (Required)): The manuscript describes the effects of small molecule surfactants on the PM organization and on TORC2 activity. This is an important set of observation that helps understanding the response of cells to environmental stressors that affect the PM. This field of study is very challenging because of the limited tools available to directly observe lipids and their movements. I consider the data and most of its interpretations of high importance, but I am not convinced of the larger model that tries to link the ergosterol data with TORC2 activity. With adjustments of the model or additional experimental support, this manuscript will be of general interest for cell biologists, especially for researchers studying membrane stress response pathways.

Response:

We thank the reviewer for highlighting the importance of studying PM stress responses and acknowledging the technical challenges involved. We hope the applied changes and additional data succeed in softening our claims about TORC2 regulation while convincing the reviewer that free sterol levels at the PM are one of several contributing factors that correlate with changes in TORC2 activity.

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Shao, C., Novakovic, V.A., Head, J.F., Seaton, B.A., Gilbert, G.E., 2008. Crystal Structure of Lactadherin C2 Domain at 1.7Å Resolution with Mutational and Computational Analyses of Its Membrane-binding Motif*. J. Biol. Chem. 283, 7230-7241. https://doi.org/10.1074/jbc.M705195200

Shi, J., Heegaard, C.W., Rasmussen, J.T., Gilbert, G.E., 2004. Lactadherin binds selectively to membranes containing phosphatidyl-L-serine and increased curvature. Biochim. Biophys. Acta 1667, 82-90. https://doi.org/10.1016/j.bbamem.2004.09.006

Souza, C.M., Schwabe, T.M.E., Pichler, H., Ploier, B., Leitner, E., Guan, X.L., Wenk, M.R., Riezman, I., Riezman, H., 2011. A stable yeast strain efficiently producing cholesterol instead of ergosterol is functional for tryptophan uptake, but not weak organic acid resistance. Metab. Eng. 13, 555-569. https://doi.org/10.1016/j.ymben.2011.06.006

Stefan, C.J., Audhya, A., Emr, S.D., 2002. The yeast synaptojanin-like proteins control the cellular distribution of phosphatidylinositol (4,5)-bisphosphate. Mol. Biol. Cell 13, 542-557. https://doi.org/10.1091/mbc.01-10-0476

Tong, J., Manik, M.K., Im, Y.J., 2018. Structural basis of sterol recognition and nonvesicular transport by lipid transfer proteins anchored at membrane contact sites. Proc. Natl. Acad. Sci. 115, E856-E865. https://doi.org/10.1073/pnas.1719709115

Topolska, M., Roelants, F.M., Si, E.P., Thorner, J., 2020. TORC2-Dependent Ypk1-Mediated Phosphorylation of Lam2/Ltc4 Disrupts Its Association with the β-Propeller Protein Laf1 at Endoplasmic Reticulum-Plasma Membrane Contact Sites in the Yeast Saccharomyces cerevisiae. Biomolecules 10, 1598. https://doi.org/10.3390/biom10121598

Torra, J., Campelo, F., Garcia-Parajo, M.F., 2024. Tensing Flipper: Photosensitized Manipulation of Membrane Tension, Lipid Phase Separation, and Raft Protein Sorting in Biological Membranes. J. Am. Chem. Soc. 146, 24114-24124. https://doi.org/10.1021/jacs.4c08580

Uekama, N., Aoki, T., Maruoka, T., Kurisu, S., Hatakeyama, A., Yamaguchi, S., Okada, M., Yagisawa, H., Nishimura, K., Tuzi, S., 2009. Influence of membrane curvature on the structure of the membrane-associated pleckstrin homology domain of phospholipase C-δ1. Biochim. Biophys. Acta BBA - Biomembr. 1788, 2575-2583. https://doi.org/10.1016/j.bbamem.2009.10.009

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Referee #3

Evidence, reproducibility and clarity

The authors describe the effects of surfactant-like molecules on the plasma membrane (PM) and its associated TORC2 complex. Addition of the surfactants with a positively-charged headgroup and a hydro-carbon tail of at least 16 caused the rapid clustering of PI-4,5P2 together with PI-4P and phosphatidylserine in large membrane invaginations. The authors convincingly demonstrate that this effect of the surfactants on the PM is likely caused by a direct disturbance of the PM organization and/or lipid composition. Interestingly, upon PalmC treatment, free ergosterol of the PM was found to first concentrate in the clusters, but within <5min this ergosterol seemed to be transported into intracellular structures, causing an overall loss in free ergosterol of the PM. The authors speculate that the initial spike in free ergosterol might be the trigger for the shutdown of TORC2 signaling. The PalmC-triggered transport of free ergosterol from the PM to intracellular structures required the lipid transport proteins Lam2/4. Loss of these transporters caused a delay in TORC2 reactivation, supporting the idea that ergosterol transport out of the PM plays a role in the recovery of normal PM organization. Hyperosmotic shock mimics some of the effects observed with PamlC, but unlike PalmC treatment, TORC2 recovery after hyperosmotic shock is not dependent on Lam2/4.

The presented data are of high quality and most conclusions are well supported. However, based on the presented data the model that a PalmC-triggered increase in free ergosterol is the cause of TORC2 inactivation is not obvious to me. The kinetics of the changes in free ergosterol levels and the changes in TORC2 activity do not match. Ergosterol is rapidly depleted after PalmC treatment (<5min) whereas TORC2 activity requires 30min to recover. Also, the hyperosmotic data on free ergosterol levels and TORC2 activity do not match. In fact, the presence of the large PM invaginations is a better predictor of TORC2 activity. The Lam2/4 data support the idea that ergosterol transport plays a role in the TORC2 recovery, but what role this is, is not clear to me. I think the data fit better with a model in which PalmC causes low tension of the PM which in turn disrupts normal lipid organization and thus causes TORC2 to shut down, maybe not by changes in free ergosterol but by changes, for instance, in lipid raft formation (which is in part effected by ergosterol levels). The transport of ergosterol is only one mechanism that is involved in restoring PM tension and TORC2 activity. However, sensing free ergosterol alone is most likely not the mechanism explaining how TORC2 senses PM tension. Therefore, I recommend that the model is revised (or supported by more data), reflecting the fact that free ergosterol levels do not directly correlate with the TORC2 activity, but instead might be only one of the PM parameters that regulate TORC2.

Further comments:

• If TORC2 is indeed inhibited by free ergosterol, the addition of ergosterol to the growth medium should be able to trigger similar effects as PalmC. If this detection of free ergosterol is very specific (e.g. if TORC2 has a binding pocket for ergosterol) we would expect that addition of other sterols such a cholesterol or ergosterol precursors should not inhibit TORC2.
• The experiment in Figure 1C is not controlled for differences in membrane intercalation of the different compounds. For instance, does C16 choline and C16 glycine accumulate at the same rate in the PM (measure similar to experiment in Figure 1B). Maybe the positive charge at the headgroup of the surfactants increases the local concentration at the PM and therefore can explain the difference in effect on the PM.
• Are the intracellular ergosterol structures associated (or in close proximity) with lipid droplets (ergosterol being modified and delivered into a lipid droplet)?
• How does the AA and DD mutations in Lam2/4 change the localization of the ergosterol sensor (before and after PalmC treatment).
• Does Lam2/4 localize to ER-PM contact sites near the large PM invaginations, which could allow for efficient transport of the free ergosterol that accumulates in these structures.

Significance

The manuscript describes the effects of small molecule surfactants on the PM organization and on TORC2 activity. This is an important set of observation that helps understanding the response of cells to environmental stressors that affect the PM. This field of study is very challenging because of the limited tools available to directly observe lipids and their movements. I consider the data and most of its interpretations of high importance, but I am not convinced of the larger model that tries to link the ergosterol data with TORC2 activity. With adjustments of the model or additional experimental support, this manuscript will be of general interest for cell biologists, especially for researchers studying membrane stress response pathways.

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Referee #2

Evidence, reproducibility and clarity

This manuscript describes multiple effects of positively-charged membrane-intercalating amphipaths (palmitoylcarnitine, PalmC, in particular) on TORC2 in yeast plasma membranes. It is a "next step" in the Loewith laboratory's characterization of the effect of this agent on this system. The study confirms the findings of Riggi et al.(2018) that PalmC inhibits TORC2 and drives the formation of membrane invaginations that contain phosphatidylinositol-bis-phosphate (PIP2) and other anionic phospholipids. It also demonstrates that PalmC intercalates into the membrane, acts directly (rather than through secondary metabolism) and is representative of a class of cationic amphipaths. The interesting finding here is that PalmC causes a rapid initial increase in the plasma membrane ergosterol accessible to the DH4 sterol probe followed by a decrease caused by its transfer to the cytoplasm through its transporter, LAM2/4. TORC2 is implicated in these processes.

Loewith et al. have pioneered in this area and this study clearly shows their expertise. Several of the findings reported here are novel. However, I am concerned that PalmC may not be revealing the physiology of the system but rather adding tangential complexity. (This concern applies to the precursor studies using PalmC to probe the TORC2 system.) In particular, I am not confident that the data justify the authors' conclusions "...that TORC2 acts in a feedback loop to control active sterol levels at the PM and [the results] introduce sterols as possible TORC2 signalling modulators."

Major issues

1. The invaginations induced by PalmC may not be physiologic but simply the result of the well-known "bilayer couple" bending of the bilayer due to the accumulation of cationic amphipaths in the inner leaflet of the plasma membrane bilayer which is rich in anionic phospholipids. Such unphysiological effects make the observed correlation of invagination with TORC2 inhibition etc. hard to interpret.
2. Electrostatic/hydrophobic association of PIP2 with PalmC could sequester the anionic phospholipid(s). Such associations could also drive the accumulation of PIP2 in the invaginations. This could explain PalmC inhibition of TORC2 through a simple physical rather than biological process. So, it is difficult to draw any physiological conclusion about PIP2 from these experiments.
3. As the authors point out, a large number of intercalated amphipaths displace sterols from their association with bilayer phospholipids. This unphysiologic mechanism can explain how PalmC causes the transient increase in the availability of plasma membrane ergosterol to the D4H probe and its subsequent removal from the plasma membrane via LAM2/4. TORC2 regulation may not be involved. In fact,the authors say that "TORC2 inhibition, and thereby Lam2/4 activation, cannot be the only trigger for PalmC induced sterol removal." Furthermore, the subsequent recovery of plasma membrane ergosterol could simply reflect homeostatic responses independent of the components studied here.

3a. The data suggest that LAM2/4 mediates the return of cytoplasmic ergosterol to the plasma membrane. To my knowledge, this is a nice finding that not been reported previously and is worth confirming more directly. 4. I agree with the authors that "It is unclear if the excess of free sterols itself is part of the inhibitory signal to TORC2..." Instead, the inhibition of TORC2 by PalmC may simply result from its artifactual aggregation of the anionic phospholipids (especially, PIP2) needed for TORC2 activity. This would not be biologically meaningful. If the authors wish to show that accessible ergosterol inhibits TORC2 activity or vice versa, they should use more direct methods. For example, neutral amphipaths that do not cause the aforementioned PalmC perturbations should still increase plasma membrane ergosterol and send it through LAM2/4 to the ER. 5. The mechanistic relationship between TORC2 activity and ergosterol suggested in the the title, abstract and discussion is not secure. I agree with the concluding section of the manuscript called "Limitations of the study". It highlights the need for a better approach to the interplay between TORC2 and ergosterol.

Minor issue

Based on earlier work using the reporter fliptR, the authors claim that PalmC reduces membrane tension. They should consider that this intercalated dye senses many variables including membrane tension but also lipid packing. I suspect that, by intercalating into and thereby altering the bilayer, PalmC is affecting the latter rather than the former.

Referees cross-commenting

Reviewers #1 and #3 were much more impressed by this study than I was. I am not a yeast expert and so I may have missed or confused something. I would therefore welcome their expert feedback regarding my comments (#2). Ted Steck

Significance

This is an interesting topic. However, use of the exogenous probe, palmitoylcarnitine, could be causing multiple changes that complicate the interpretation of the data.

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Referee #1

Evidence, reproducibility and clarity

This is a very well conceived study of responses to plasma membrane stresses in yeast that signal through the conserved TORC2 complex.

Physical stress through small molecular intercalators in the plasma membrane is shown to be independent of their biochemistry and then studies for its effect on plasma membrane morphology and the distribution of free ergosterol (the yeast equivalent of cholesterol), with free being the pool of cholesterol that is available to probes and/or sterol transfer proteins. Experiments nicely demonstrate a negative feedback loop consisting of: stress -> increased free sterol and TORC2 inhibition -> activation of LAM proteins (as demonstrated by Relents and co-workers previously) -> removal of free sterol -> return to unstressed state of PM and TORC2.

Comments

Fig 2A: Is detection of PIP/PIP2/PS linear for target, or possibly just showing availability that is increased due to local positive curvature?

Can any marker be identified for the D4H spots at 2 minutes? In particular, are they early endosomes (shown by brief pre-incubation with FM4-64)?

Is there any functional (& direct) link between Arp inhibition (as in the Pombe study of LAMs by the lab of Sophie Martin) and PM disturbance by amphipathic molecules ?

Minor

Fig 2A: Labels not clear. Say for each part what FP is used for pip2. Move fig s2d to main ms. The 1 min and 2 min data are integral to the story

The role of Lam2 and Lam4 in retrograde sterol transport has in vivo only been linked to one of their two StART domains not both, as mentioned in the text.

Throughout, images of tagged D4H should be labelled as such, not as "Ergosterol".

Significance

These results in budding yeast are likely to be directly applicable to a wide range of eukaryotic cells, if not all of them. I expect this paper to be a significant guid elf research in this area.

The paper specifically points out that the current experiments do not distinguish the precise causation among the two outcomes of stress: increased free sterol and TORC2 inhibition. Of these two outcomes which causes which is not yet known. If data were added that shed light on this causation that would make this work much more signifiant, but I can understand 100% that this extra step lies beyond - for a later study for which the current one forms the bedrock.

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Reply to the reviewers

We thank all the reviewers for their helpful and constructive comments and for their time.

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

Summary: Dady et al have developed fluorescent reporters to enable live imaging of cell behaviour and morphology in human pluripotent stem cell lines (PSCs). These reporters target 3 main features, the plasma membrane, nucleus and cytoskeleton. Reporter PSCs have been generated using a piggyBac transposon-mediated stable integration strategy, using a hyperactive piggyBac transposase (HyPBase). The same constructs were also used for mosaic labelling of cells within 2D cultures using lipofectamine transfection.

The reporters used are tagged with either eGFP or mKate2 (far red) and tag the plasma membrane (pm) via the addition of a 20 amino-acid sequence from rat GAP-43 to the N-terminus of the fluorescent protein, the nucleus via Histone 2B with a laser-mediated photo-conversion option (H2B-mEos3.2), and the cytoskeleton via F-Tractin. In total, the authors produced lines with the following:

• pm-mKate2 (far red) • pm-eGFP (green) • H2B-mEos3.2 (green to red) • F-tractin-mKate2 (far red) • H2B-mEos3.2 and pm-mKate2 (green to red, plus far red)

The cell lines used to generate these were the human embryonic stem cell line H9 and human induced pluripotent cell line ChiPS4. The constructs were also used to label cells in a mosaic fashion, using lipofectamine transfection of the original cell lines once they had formed neural rosettes.

Using these cells, Dady et al then performed live imaging in vitro of human spinal cord rosettes and assessed cell behaviour. In particular they analysed mitotic cleavage planes and apical positioning of neural progenitor cells (NPCs), and assessed actin dynamics within these cells. They showed a slowing of the cell cycle length after the initial expansion phase, an increase in the rate of asymmetric division of these NPCs, and abscission of the apical membrane during these divisions. The F-tractin reporter showed enrichment at the basal nuclear membrane during these cell divisions, suggested to help prevent basal chromosome displacement during mitosis.

Major comments: The data presented are convincing and could be strengthened by the following additions and clarifications:*

2. How long do the fluorescent reports take to be visible when transfected via lipofectamine? How efficiently are they expressed? And what concentrations were tested to enable the mosaic expression presented? * We followed the manufacturer’s instructions for Lipofectamine 3000 transfection, using the protocol recommended for set up for a 6 wells plate. We detected fluorescence the following morning ~16h. We did not assess earlier time points or optimise efficiency as we observed the mosaic pattern of expression we set out to achieve, with small groups of labelled cells and single cells as shown in Figure 3 and movies 2 and 3. This information and the detailed protocol provided below are now included in the Methods section “Labelling individual cells in human spinal cord rosettes by lipofection”.

Manufacturer’s instructions for Lipofectamine 3000 transfection (6 well plate):

• 1 tube containing 125 ul of Opti-MEM and 7.5 ul of Lipofectamine 3000
• 1 tube containing 250 ul of Opti-MEM with 5 ug of DNA (total mix DNAs of 2 ug/ul) and P3000 Reagent
• Add diluted DNA to diluted Lipofectamine 3000 (Ratio 1:1) and incubate for 10 to 15 min at Room Temperature.
• 20 ul of DNA-Lipid complex was added to neural rosettes growing in 8 well IBIDI dishes (20 ul/well).
• The ratio of DNA (PiggyBac plasmid) and HypBase transposase was kept at 5:1 (for a final concentration of 2ug/ul).

• Cells in IBIDI dishes were left to develop in a sterile incubator overnight and mosaic fluorescence was observed the following morning (~16h post-lipofection).

• Will these cell lines and constructs be made publicly available after publication?*

The cell lines can be made available: for those reporters made in the H9 WiCell line an MTA will first have to be signed between the requesting PI and WiCell and permission for us to share the line(s) confirmed by WiCell; similarly, for reporters in ChiPS4 line an MTA will first need to be signed between the requesting PI and Cellartis/TakaraBio Europe. We will need to make a charge to cover costs. Constructs will be deposited with Addgene.

• Were the H9 and ChiPS4 lines characterised after the reporters were added to show they still proliferate/differentiate as they did prior to the reporter integration*?

In the Results we make clear that all lines created are polyclonal, with exception of a pm-eGFP ChiPS4 line, which is a monoclonal line (lines 145-150). We do not have direct data measuring cell proliferation but collected cell passaging data for all the reporter lines. This showed that they grow to similar densities at each passage compared to the parental line (this metadata is now provided as Supplementary data 1 and is cited in the Methods, line 348).

As a proof of principle for this approach, we created one monoclonal line from a polyclonal line ChIPS4-pm-eGFP. The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers (immunocytochemistry data Figure S4), and the ability to differentiate into 3 germ layers (qPCR Supplementary data 1). This information is already cited in the Methods (Lines 358-362).

• Can the novel actin dynamics described be quantified? How many cells imaged show these novel dynamics?* Some of this quantification data was already reported in the paper (in figure 4 legend and in the Methods); we have now updated this and provide the detailed metadata in an Excel spread sheet, Supplementary data 4 (cited in the Methods, line 489)

Minor comments: 1. Some images in the figures and supplemental movies are low in resolution, for example the DAPI in Fig 4B, making it hard to distinguish individual cells. Please increase this.

We consider the DAPI labelling in Figure 4b to be clear, however, we wonder whether the reviewer was expecting to also see this combined with the other markers. We have therefore now provided these merged additional images in a revised Figure 4.

• Please show a merge of Phalloidin and F-Tractin in Fig4, this will help the colocalization to be fully appreciated.*

This has now been provided in revised Figure 4B.

• Some additional annotation on the supplemental movies would be useful to indicate to the **reader exactly what cell to follow. *

We have added indicative arrows to the movies, and note that more detailed labelling of the series of still images from these movies are provided in the main figures (Figures 3D and 4E & F).

*Reviewer #1 (Significance (Required)):

Human neurogenesis is currently poorly understood compared to many model systems used, yet key differences have already been identified between the human and the mouse, prompting the need for further investigation of human neural development. A major reason that human neurogenesis has been difficult to study is a lack of tools to enable cell morphology and behaviours to be analysed in real time.

The reporters and reporter PSC lines generated by Dady et al will allow many of these cell characteristics to be observed using live imaging. For example, the morphology of neural progenitors during and after cell divisions, how the apical and basal processes and membranes are divided, and how the actin cytoskeleton helps to regulate these processes.

*Importantly, PSC lines can be very heterogeneous, making generating reporter lines costly and time intensive. The use of these reporters with lipofectamine transfection, for a mosaic labelling, allows the visualisation of the plasma membrane, nucleus and cytoskeleton in any human PSC/NPC line, or even in human tissue cultures, without the need to generate each specific reporter line, making it a valuable tool for many labs in the field.

We strongly agree with this final point; this is a major reason for our study.

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

The manuscript describes the generation of novel lines of human pluripotent stem cells bearing fluorescent reporters, engineered through piggyBac transposon-mediated integration. The cells are differentiated into neuronal organoids, allowing to capture cellular behaviors associated to cell division. A replating protocol allows the observation of aging neurons by reducing the thickness of the tissue thereby facilitating live imaging. The authors also leverage the transposon technology to create mosaically-labelled organoids which allows visualizing aspects of neuronal delamination, notably cytoskeleton dynamics. They discover an undescribed pattern of F-actin enrichment at the basal nuclear membrane prior to nuclear envelope breakdown.

L104-109: "Moreover, the transposon system obviates drawbacks of directly engineering endogenous proteins...". Despite the risk of endogenous protein dysfunction, directly tagging allows the full regulation of gene expression (including the promoter, the enhancers and other regulatory regions rather than a strong constitutive promoter such as CAG). In addition, the number of copies integrated and the genomic regions are variable with PB, which does not reflect the endogenous expression. This could be rephrased by nuancing the advantages and drawbacks of each approach. The PiggyBac method is easier and faster, but it results in overexpression of a tagged protein that will be expressed since the hESC state and might not reflect the expression dynamics of the endogenous protein.* We agree and have now revised this in the Introduction L109-118.

*L124-126: "To monitor cell shape and dynamics we used a plasma membrane (pm) localized protein tagged with eGFP or mKate2 (pm-eGFP or pm-mKate2)." Could the authors provide more details and a reference on the palmitoylated rat peptide use to force membrane expression? *

This information, including the peptide sequence, is provided in the Methods (L330-331), we have now added a reference addressing its role in membrane localisation PMID: 2918027.

L132-133: " Finally, to observe actin cytoskeletal dynamics we selected F-tractin, for its minimal impact on cytoskeletal homeostasis".

A recent JCB paper (https://doi.org/10.1083/jcb.202409192) suggests that "F-tractin alters actin organization and impairs cell migration when expressed at high levels". Whether the overexpression of F-tractin in hESC using a CAG promoter reflects the physiological F-actin dynamics and/or if the high levels could lead to an alteration of cell behavior should be addressed or at least discussed. The paper we cite in this sentence (Belin et al 2014) evaluates F-tractin expression against other approaches to labelling and monitoring the actin cytoskeleton and concludes that in comparison F-tractin has minimal impact.

We do appreciate that expression above the endogenous level has the potential to alter cell behaviour and have revised the paper to more explicitly acknowledge this: in the Introduction (L109-112), and in the Discussion/conclusion (L289-293) where we now note the recent advances reported in Shatskiy et al. 2025 PMID: 39928047.

“A further potential limitation of this approach is that over-expression driven by the CAG promoter might not reflect physiological protein dynamics and/or alter cell behaviour; for example, high levels of F-Tractin can impair cell migration and induce actin bundling, interestingly, this can now be minimised by removing the N-terminal region (Shatskiy et al 2025)”.

L146-147: "...to generate polyclonal cell lines selected for expression of easily detectable (medium level) fluorescence for live imaging studies". What are the criteria used to define medium level? Number of copies integrated into the genome? Or levels by FACS during clone selection?

To clarify, all the lines presented here are polyclonal, except for one clonal line, pm-eGFP in ChiPS4. The numbers of copies integrated may vary from cell to cell in polyclonal lines. In this study, we selected cells for all lines with a FACS gate and this data is presented in Figure S1 (see line 147).

L260-263: "Efficient stable integration and moderate expression levels were achieved by optimising, i) the quantity and ratio of piggyBac plasmids and transposase and ii) subsequent FACS to exclude high expressing cells, as well as iii) transfection methods, including temporally defined lipofection in hiPSC-derived tissues." The ration 5:1 is classically used for PB Transposase delivery, however there is still high variability in the number of copies integration. Lipofection in derived tissues has been shown to be challenging. Could the authors should provide quantitative data regarding the efficiency of their approaches, notably the level of mosaicism one could expect?

We provide quantitative data for the efficiency of transfection using nucleoporation assays (FACS data presented in Supplementary figure S1), which shows more than 80-90% efficiency for eGFP in 82.82% of cells, mKate2 in 92.74% of cells, and H2B-mEos3 22.75% of cells, while 13.79% of cells co-expressed pm-Kate and H2B-mEos3.2. No comparative data regarding the efficiency of the tissue Lipofection assay was collected: our goal was to label single/small numbers of cells in order to monitor individual cell behaviours, and this “inefficient labelling” was readily achieved following the manufacturer’s instructions (please see response to Review 1 point 1), further details are now provided in the Methods.

L191-194: "We further wished to monitor sub-cellular behaviour within the developing neuroepithelium. To achieve this, we devised a strategy to target a mosaic of cells in established neural rosettes using lipofection. PiggyBac constructs and HyPBase transposase were transfected into D8/D9 human spinal cord neural progenitors using lipofectamine (Felgner, et al., 1987)(Fig. 3A)." The mosaicism is not an all or nothing in this method but also leads to variations in expression levels among the positive cells. The protocol for lipofection could be better detailed to allow easy reproduction by other teams, and its expected efficiency should be discussed. It would be interesting to explore the relationship between individual cells phenotype and expression levels. Please see response to Reviewer 1 point 1 above for more detailed lipofection protocol which generated mosaic expression, this is now also included in the Methods. We agree that investigating the relationship between individual cell phenotypes and expression levels would be interesting, but we think this is beyond the scope of this paper.

Additional comments: -Did the authors perform karyotyping of the hPSCs prior to use in the differentiation protocol?

As these are polyclonal lines, we did not undertake karyotyping. This could be done for the one monoclonal line described here (pm-eGFP ChiPS4 line): we lack funds for commercial options, but we are exploring other possibilities.

-Were pluripotency assays performed after reporter lines generation?

These were carried out for the clonal pm-eGFP ChiPS4 line (lines 145-150). The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers by IF (Figure S4), and the ability to differentiate into 3 germ layers by qPCR (Supplementary data 2). This information is provided in the Methods (Lines 358-362).

*-Did the authors measure the cell proliferation rate in H2B-overexpressing cells and controls? Since H2B plays an important role in cytokinesis, it could interfere in cell division when H2B is overexpressed (see doi: 10.3390/cells8111391). *

We did not directly measure cell division when H2B is over-expressed. However, we assessed cell -passaging time of all the transfected cell lines. This showed that they grow to similar densities at each passage compared to the parental line (this is now provided as Supplementary data 1 and is cited in the Methods, line 348). We also found no difference between apical visiting time of progenitors in spinal cord rosettes expressing pm-eGFP or H2B-mEoS3.2, further supporting the conclusion that levels of H2B-mEoS3.2 expression achieved in this line did not interfere with cell division (metadata provided in Supplementary data 3).

The authors should provide data concerning the efficiency of expression of the distinct markers after electroporation. This is provided in Supplementary Figure S1 (FACS data) and detailed above for this reviewer.

*At Fig 1C, the schematic representation describes clone selection, however in the methods it is stated (L348-349): "Sorted cells expressing medium levels of fluorescence were expanded and frozen then representative lots of each polyclonal cell line...". There is some confusion regarding which experiments were performed using polyclonal medium-level mixed populations or monoclonal populations. *

We apologise for any confusion and have revised the Figure 1C schematic to indicate that cells can be selected to either make polyclonal lines or clonal lines.

*Reviewer #2 (Significance (Required)):

The study provides novel tools, as well as elements regarding neuroepithelium biology. It is well conducted and written, and the quality of images is excellent. It reads more as a resource paper in its current version, since the observation regarding neural cell division and delamination are interesting but not deeply explored, so this review will focus on those technical aspects rather than the novelty of the biological findings.

This study would be of interests for researchers in stem cells and organoids, developmental biology, and neurosciences.

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

In the manuscript, "Engineering fluorescent reporters in human pluripotent cells and strategies for live imaging human neurogenesis" the authors Dady et al. describe the adaptation of a recent advancement in transposase technology (HyPBase) as a method to integrate live reporters in human pluripotent stem cells. They show that these florescent reporters paired with new imaging strategies can be used to confirm the existence cellular behaviour described in other species such as the interkinetic nuclear migration (IKNM) of dividing progenitors in neural tube development. Finally, they demonstrate that this live imaging system is also able to discover novel biology by identifying previously undescribed actin polymerization at the basal nuclear surface of cortical progenitors undergoing cell division. Overall, the study presents two examples in which this adapted tool will aid in live-imaging studies of cellular biology.

Major Concerns: 1. This work needs more controls to properly demonstrate claims that their engineering strategy provides an advancement to current Piggyback methods. Their HyPBase strategy needs to be compared and quantified in terms of efficiency with other methods to support their claims (increased detection and reduced phototoxicity).*

We do not make specific claims for our experiments with respect to the superiority of HyPBase strategy. Our comments on this approach referred to by the reviewer here are in the Introduction (L 94-103), are supported by the literature (e.g. more stable gene expression than native piggyBac or the Tc1/mariner transposase Sleeping Beauty (Doherty, et al., 2012, Yusa, et al., 2011) and serve to explain our selection of HyPBase for our experiments. We make a case for using HyPBase as opposed to another transposase and although it would be interesting to compare efficiencies, this comment does not specify what “other methods” might be informative.

2.Throughout the manuscript more quantification is needed of the results. How many rosettes were examined? Were all the reported cells within one rosette? Were there differences between rosettes? This should be done for both the spinal and cortical differentiations.

The reviewer appears to have missed this information – we placed detailed quantifications in the figure legends (numbers of independent experiments and rosettes) and in the Methods in a specific section on Quantification of cell behaviour (L465-486), rather than in the main text. These has since been further updated and we now also provide additional metadata in the form of Excel spreadsheets for quantifications and analyses made for both spinal cord and cortical rosettes (Supplementary data 3 and 4 respectively).

Minor Comments: 1. Line 246 needs quantification shown in figures of the statements made. Specifically, how many cells were measured to get this number?

This information was provided in the figure 4 legend and we have since added numbers to these data; we were able to monitor 169 divisions in 21 rosettes; 154/166 divisions had vertical cleavage planes (symmetric) and 12/166 had horizontal cleavage planes (asymmetric).

These detailed observations were made in two independent experiments, along with observations of basal nuclear membrane F-Tractin localisation. This is noted in figure 4 legend, Methods and detailed metadata is provided in Supplementary data 4.

2.How many cells in the cortical rosettes had the enriched actin at the basal nuclear surface?

We confidently observed basal nuclear membrane F-Tractin enrichment in 141/146 divisions, for the remaining 20 cases (166-146), we could not tell whether F-Tractin is enriched or not at the basal nuclear membrane either because of low expression levels or because the basal nuclear membrane was out of focus at NEB. In 5 cases, we did not see the basal nuclear enrichment despite sufficient F-Tractin expression levels and the nucleus being in focus. We have updated the Fig4 legend excluding the non-analysable cases and see detailed metadata is provided in Supplementary data 4.

*Reviewer #3 (Significance (Required)):

General Assessment: This manuscript makes a very minor advancement in the field of stem cell engineering and developmental biology, but one that is worthy of publication with a few edits.

Advance: While PiggyBac reporters are widely used in stem cell engineering, Dady et al. demonstrate a new workflow using HyPBase which would be beneficial to the field. However, to increase this benefit, much more description and quantification of the methods would be needed. The biological advances of this manuscript are also very minor, but interesting as most of them confirm that human neural rosettes mimic many of the observed cell behaviours seen in animal models. Along these lines is the actin dynamics observation in cortical rosettes is interesting, but a preliminary observation and in need of follow up experiments.

Audience: Regardless, this technique would be of interest to the wider field of stem cell engineering.

My Expertise: Human Stem Cell Engineering, Neural Tube Development*

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Referee #3

Evidence, reproducibility and clarity

In the manuscript, "Engineering fluorescent reporters in human pluripotent cells and strategies for live imaging human neurogenesis" the authors Dady et al. describe the adaptation of a recent advancement in transposase technology (HyPBase) as a method to integrate live reporters in human pluripotent stem cells. They show that these florescent reporters paired with new imaging strategies can be used to confirm the existence cellular behaviour described in other species such as the interkinetic nuclear migration (IKNM) of dividing progenitors in neural tube development. Finally, they demonstrate that this live imaging system is also able to discover novel biology by identifying previously undescribed actin polymerization at the basal nuclear surface of cortical progenitors undergoing cell division. Overall, the study presents two examples in which this adapted tool will aid in live-imaging studies of cellular biology.

Major Concerns:

1.This work needs more controls to properly demonstrate claims that their engineering strategy provides an advancement to current Piggyback methods. Their HyPBase strategy needs to be compared and quantified in terms of efficiency with other methods to support their claims (increased detection and reduced phototoxicity). 2.Throughout the manuscript more quantification is needed of the results. How many rosettes were examined? Were all the reported cells within one rosette? Were there differences between rosettes? This should be done for both the spinal and cortical differentiations

Minor Comments:

1.Line 246 needs quantification shown in figures of the statements made. Specifically how many cells were measured to get this number? 2.How many cells in the cortical rosettes had the enriched actin at the basal nuclear surface?

Significance

General Assessment: This manuscript makes a very minor advancement in the field of stem cell engineering and developmental biology, but one that is worthy of publication with a few edits.

Advance: While PiggyBac reporters are widely used in stem cell engineering, Dady et al. demonstrate a new workflow using HyPBase which would be beneficial to the field. However, to increase this benefit, much more description and quantification of the methods would be needed. The biological advances of this manuscript are also very minor, but interesting as most of them confirm that human neural rosettes mimic many of the observed cell behaviours seen in animal models. Along these lines is the actin dynamics observation in cortical rosettes is interesting, but a preliminary observation and in need of follow up experiments.

Audience: Regardless, this technique would be of interest to the wider field of stem cell engineering.

My Expertise: Human Stem Cell Engineering, Neural Tube Development

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Referee #2

Evidence, reproducibility and clarity

The manuscript describes the generation of novel lines of human pluripotent stem cells bearing fluorescent reporters, engineered through piggyBac transposon-mediated integration. The cells are differentiated into neuronal organoids, allowing to capture cellular behaviors associated to cell division. A replating protocol allows the observation of aging neurons by reducing the thickness of the tissue thereby facilitating live imaging. The authors also leverage the transposon technology to create mosaically-labelled organoids which allows visualizing aspects of neuronal delamination, notably cytoskeleton dynamics. They discover an undescribed pattern of F-actin enrichment at the basal nuclear membrane prior to nuclear envelope breakdown.

L104-109: "Moreover, the transposon system obviates drawbacks of directly engineering endogenous proteins...". Despite the risk of endogenous protein dysfunction, directly tagging allows the full regulation of gene expression (including the promoter, the enhancers and other regulatory regions rather than a strong constitutive promoter such as CAG). In addition, the number of copies integrated and the genomic regions are variable with PB, which does not reflect the endogenous expression. This could be rephrased by nuancing the advantages and drawbacks of each approach. The PiggyBac method is easier and faster, but it results in overexpression of a tagged protein that will be expressed since the hESC state and might not reflect the expression dynamics of the endogenous protein.

L124-126: "To monitor cell shape and dynamics we used a plasma membrane (pm) localized protein tagged with eGFP or mKate2 (pm-eGFP or pm-mKate2)." Could the authors provide more details and a reference on the palmitoylated rat peptide use to force membrane expression?

L132-133: " Finally, to observe actin cytoskeletal dynamics we selected F-tractin, for its minimal impact on cytoskeletal homeostasis..". A recent JCB paper (https://doi.org/10.1083/jcb.202409192) suggests that "F-tractin alters actin organization and impairs cell migration when expressed at high levels". Whether the overexpression of F-tractin in hESC using a CAG promoter reflects the physiological F-actin dynamics and/or if the high levels could lead to an alteration of cell behavior should be addressed or at least discussed.

L146-147: "...to generate polyclonal cell lines selected for expression of easily detectable (medium level) fluorescence for live imaging studies". What are the criteria used to define medium level? Number of copies integrated into the genome? Or levels by FACS during clone selection?

L260-263: "Efficient stable integration and moderate expression levels were achieved by optimising, i) the quantity and ratio of piggyBac plasmids and transposase and ii) subsequent FACS to exclude high expressing cells, as well as iii) transfection methods, including temporally defined lipofection in hiPSC-derived tissues." The ration 5:1 is classically used for PB Transposase delivery, however there is still high variability in the number of copies integration. Lipofection in derived tissues has been shown to be challenging. Could the authors should provide quantitative data regarding the efficiency of their approaches, notably the level of mosaicism one could expect?

L191-194: "We further wished to monitor sub-cellular behaviour within the developing neuroepithelium. To achieve this, we devised a strategy to target a mosaic of cells in established neural rosettes using lipofection. PiggyBac constructs and HyPBase transposase were transfected into D8/D9 human spinal cord neural progenitors using lipofectamine (Felgner, et al., 1987)(Fig. 3A)." The mosaicism is not an all or nothing in this method but also leads to variations in expression levels among the positive cells. The protocol for lipofection could be better detailed to allow easy reproduction by other teams, and its expected efficiency should be discussed. It would be interesting to explore the relationship between individual cells phenotype and expression levels.

Additional comments:

• Did the authors perform karyotyping of the hPSCs prior to use in the differentiation protocol?
• Were pluripotency assays performed after reporter lines generation?
• Did the authors measure the cell proliferation rate in H2B-overexpressing cells and controls? Since H2B plays an important role in cytokinesis, it could interfere in cell division when H2B is overexpressed (see doi: 10.3390/cells8111391). The authors should provide data concerning the efficiency of expression of the distinct markers after electroporation. At Fig 1C, the schematic representation describes clone selection, however in the methods it is stated (L348-349): "Sorted cells expressing medium levels of fluorescence were expanded and frozen then representative lots of each polyclonal cell line...". There is some confusion regarding which experiments were performed using polyclonal medium-level mixed populations or monoclonal populations.

Significance

The study provides novel tools, as well as elements regarding neuroepithelium biology. It is well conducted and written, and the quality of images is excellent. It reads more as a resource paper in its current version, since the observation regarding neural cell division and delamination are interesting but not deeply explored, so this review will focus on those technical aspects rather than the novelty of the biological findings.

This study would be of interests for researchers in stem cells and organoids, developmental biology, and neurosciences.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Dady et al have developed fluorescent reporters to enable live imaging of cell behaviour and morphology in human pluripotent stem cell lines (PSCs). These reporters target 3 main features, the plasma membrane, nucleus and cytoskeleton. Reporter PSCs have been generated using a piggyBac transposon-mediated stable integration strategy, using a hyperactive piggyBac transposase (HyPBase). The same constructs were also used for mosaic labelling of cells within 2D cultures using lipofectamine transfection.

The reporters used are tagged with either eGFP or mKate2 (far red) and tag the plasma membrane (pm) via the addition of a 20 amino-acid sequence from rat GAP-43 to the N-terminus of the fluorescent protein, the nucleus via Histone 2B with a laser-mediated photo-conversion option (H2B-mEos3.2), and the cytoskeleton via F-Tractin. In total, the authors produced lines with the following:

• pm-mKate2 (far red)
• pm-eGFP (green)
• H2B-mEos3.2 (green to red)
• F-tractin-mKate2 (far red)
• H2B-mEos3.2 and pm-mKate2 (green to red, plus far red)

The cell lines used to generate these were the human embryonic stem cell line H9 and human induced pluripotent cell line ChiPS4. The constructs were also used to label cells in a mosaic fashion, using lipofectamine transfection of the original cell lines once they had formed neural rosettes.

Using these cells, Dady et al then performed live imaging in vitro of human spinal cord rosettes and assessed cell behaviour. In particular they analysed mitotic cleavage planes and apical positioning of neural progenitor cells (NPCs), and assessed actin dynamics within these cells. They showed a slowing of the cell cycle length after the initial expansion phase, an increase in the rate of asymmetric division of these NPCs, and abscission of the apical membrane during these divisions. The F-tractin reporter showed enrichment at the basal nuclear membrane during these cell divisions, suggested to help prevent basal chromosome displacement during mitosis.

Major comments:

The data presented are convincing and could be strengthened by the following additions and clarifications: 1. How long do the fluorescent reports take to be visible when transfected via lipofectamine? How efficiently are they expressed? And what concentrations were tested to enable the mosaic expression presented? 2. Will these cell lines and constructs be made publicly available after publication? 3. Were the H9 and ChiPS4 lines characterised after the reporters were added to show they still proliferate/differentiate as they did prior to the reporter integration? 4. Can the novel actin dynamics described be quantified? How many cells imaged show these novel dynamics?

Minor comments:

1. Some images in the figures and supplemental movies are low in resolution, for example the DAPI in Fig 4B, making it hard to distinguish individual cells. Please increase this.
2. Please show a merge of Phallodin and F-Tractin in Fig4, this will help the colocalization to be fully appreciated.
3. Some additional annotation on the supplemental movies would be useful to indicate to the reader exactly what cell to follow.

Significance

Human neurogenesis is currently poorly understood compared to many model systems used, yet key differences have already been identified between the human and the mouse, prompting the need for further investigation of human neural development. A major reason that human neurogenesis has been difficult to study is a lack of tools to enable cell morphology and behaviours to be analysed in real time.

The reporters and reporter PSC lines generated by Dady et al will allow many of these cell characteristics to be observed using live imaging. For example, the morphology of neural progenitors during and after cell divisions, how the apical and basal processes and membranes are divided, and how the actin cytoskeleton helps to regulate these processes.

Importantly, PSC lines can be very heterogeneous, making generating reporter lines costly and time intensive. The use of these reporters with lipofectamine transfection, for a mosaic labelling, allows the visualisation of the plasma membrane, nucleus and cytoskeleton in any human PSC/NPC line, or even in human tissue cultures, without the need to generate each specific reporter line, making it a valuable tool for many labs in the field.

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Reply to the reviewers

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

Comments for the authors of Review Commons Manuscript RC-2024-02804:

The author of the Review Commons manuscript "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", present their recent work evaluating hemagglutinin interactions with cellular receptors and antibodies. This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Their findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies. Below are some comments that I would like the authors to address as they revise the manuscript.

Comments:

1. Can the authors provide justification for the two influenza viruses that they used.

We selected the lab-adapted IAV strains A/WSN/1933 (H1N1) and A/Hong Kong/1968 (H3N2) for this work because they are well-studied, including in the context of the antibodies used here, S139/1 and C05. While both antibodies bind to more contemporary H3N2 strains, they no not bind to HA from pandemic H1N1. Another feature of these strains is that their HAs have high enough affinity to both antibodies to enable strong signal in our imaging assays. This context for our strain selection has been added in lines 85-88.

1. The use of filamentous particles is a strength, but authors should detail the role of filamentous vs. spherical in nature and lab settings. This will help researchers that plan to repeat these assays.

We have revised the text (lines 336-339) to include more context on the biology of filamentous and spherical influenza viruses. In our experiments, HK68 naturally produces filaments in cell culture whereas WSN33 does not. To produce filaments artificially, we replace the M1 sequence from WSN33 with that of M1 from A/Udorn/1972, an H3N2 strain that is closely related to HK68.

1. Did the authors add the Udorn M1 to the HK68 as well?

Since HK68 naturally forms filaments, we did not introduce Udorn M1 into this strain. We note that the amino acid sequences of Udorn M1 and HK68 M1 differ only at position 167 (Alanine in Udorn, Threonine in HK68), and that this residue has previously been found to not correlate with virus morphology (10.1016/j.virol.2003.12.009).

Reviewer #1 (Significance (Required)):

This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Thie findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies.

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

Summary

In this study, Benegal et al. investigate the binding kinetics of HA-head-specific antibodies (S139/1 and C05) to intact influenza virus particles using a fluorescence microscopy-based technique to measure the dissociation rate (koff) of the antibodies. By applying their proposed equilibrium model for bivalent antibody binding to HA, the authors calculated the crosslinking rate (kx), which represents the rate at which a single-bound antibody crosslinks to an additional HA molecule. Their experiments revealed that antigen crosslinking significantly slows koff, reducing it by up to two orders of magnitude. The authors further utilized streptavidin-coated beads conjugated with biotinylated HA or biotinylated BSA at varying concentrations to control HA surface density. Their results demonstrated that the two tested HA-head-specific antibodies retained the ability to crosslink HAs even at ~10-fold lower HA surface densities. In a complementary experiment, they employed an HA-anchor-specific antibody to restrict HA flexibility, which led to reduced binding of S139/1 and C05 IgGs but not their Fab fragments. This finding suggests that HA flexibility, rather than density, is the primary determinant of antibody crosslinking and avidity. Overall, the authors present an innovative approach to elucidating the dissociation and crosslinking kinetics of antibodies targeting intact virions or nanoparticles. The study is well-designed, with alternative interpretations of the results carefully considered and addressed throughout. I have only a few minor comments and suggestions for clarification.

Minor comments:

1. In Figure 1, does the grey color of each IgG in panel C indicate the Fc domain? If so, please add the description of the colors to the figure legend. In fact, it may be better to explain all the colors used here (for HA1, HA2, Fab heavy chain, light chain, etc.).

We have included this information in panel C and the caption for Figure 1.

1. Under the section," Bivalent binding of S139/1 and C05 persists after ~10-fold reductions in HA surface densities", the beginning of the second paragraph writes, "For both S139/1 and C05 Fab, binding increases linearly with HA density, as expected for a monovalent interaction dictated by absolute HA availability rather than density (Fig. 3D). Interestingly, the same relationship is observed for S139/1 IgG."

Visually, I think the same relationship also seems to hold for C05 IgG. Would it be better to perform some linear regression and report the R2 value for the fitting so that this assessment can be quantitative?

We agree with the reviewer's point. In Figure 3 of the revised manuscript, we include the results from a linear regression analysis to make this assessment more quantitative.

1. At the end of the same page, in the same paragraph, the authors mentioned, "In contrast to the IgG, Fab binding measured at twice the molar concentration of the IgG is nearly undetectable under these conditions, confirming the IgG binding is not occurring through monovalent interactions (Fig. S2E)." What are the conditions you are referring to? In Fig. S2E, there is only the Ab intensity for the Ab binding at 100% HA (and not the other percentages). For the Ab intensity of S139/1 Fab, what is the concentration of the Fab used in Figure 3D? Why could the intensity in this experiment for S139/1 Fab reach ~100,000, whereas that of the 8 nM in Fig. S2E can only reach ~20,000?

To clarify this point, we have updated Figure 3 to include the antibody concentration used for each experiment. The experiments in Fig 3 are conducted approximately around the respective KD of each IgG or Fab to ensure both consistency and strong signal-to-noise. For S139/1, we use 4nM of IgG, and 25nM of Fab. In Fig S2E, we use a concentration of Fab fragments double to that of the IgG, to reach an equivalent concentration of binding sites and confirm that the IgG binding we see is indeed due to bivalent binding. In this case, we use 4nM of IgG and 8nM of Fab.

1. Under the section, "Tilting of HA about its membrane anchor contributes to C05 and S139/1 avidity", in the second paragraph, the authors wrote, "If this is correct, we reasoned that avidity could be reduced by constraining tilting of the HA ectodomain. To test this hypothesis, we used FISW84, an antibody that binds to the HA anchor epitope and biases the ectodomain into a tilted conformation (Fig. 4B)."

Can you use some computational models (maybe the same one you used for Figure 4A) to show that when an HA trimer is bounded by FISW84 Fabs, the tilting of HA is constrained? I think this will help substantiate the assertion above.

This is an important point. The model that we employ in Figure 4A is suited to predicting the angles sampled by HAs when they are bound by an IgG antibody, but it does not take into consideration clashes with the viral membrane. It is these clashes that we predict based on published structures (reference 35 in the revised manuscript) will constrain HA tilting when FISW84 binds to the HA anchor. We have revised the text (Lines 247-249) to clarify these points.

1. It would be good if you could mention the strain of HA used in the experiments in Figure 4 in the actual Figure as well (as supposed to just in the figure legend).

We have added this information to Figure 4 in the revised manuscript.

1. I do not see a method section for the structure-based model you used in Figure 4. In the text, you cited your previous study (ref 28) for the model, but it would be good to write about this briefly (and how you specifically apply the model in this study) in this current manuscript.

We have updated the methods to include a subsection ("Geometric Model for Preferred Crosslinking Geometry") on how the structure-based model was set up, along with a corresponding visual in Fig S3 of the angles of freedom given.

1. In Figure S1 panel D, what is the unit of the antibody concentration? Could you please add it to the graph legend?

We have updated the figure (S1E in the revised manuscript) to include this information.

Reviewer #2 (Significance (Required)):

Previously, this group utilized the same fluorescence-based method to investigate the potency of anti-HA IgG1 antibodies in preventing viral entry versus egress, as well as the tendency of antibodies targeting different HA epitopes to crosslink two HA trimers in cis or in trans (He et al., J Virol, 2024). In this study, they extend their work by evaluating, in-depth, how the density and flexibility of hemagglutinin (HA) on the viral surface influence the binding avidity of anti-HA antibodies. Using two human IgG1 antibodies targeting the HA head, the authors demonstrate that these antibodies can crosslink two HA trimers in cis, even when the trimers are further apart than adjacent HAs. Notably, the study reveals that HA flexibility, rather than density, is the key determinant modulating antibody crosslinking. Even at a 10-fold reduced HA density compared to the original, the antibodies retained their ability to crosslink trimers.

This study provides critical insights into the relationship between HA density, flexibility, and antibody function, adding to the broader understanding of antibody crosslinking-a topic frequently discussed in the field of influenza research. These findings could have significant implications for vaccine design, particularly for strategies involving the display of the HA ectodomain on nanoparticles, potentially guiding the development of more effective influenza vaccines. Furthermore, the broader relevance of these findings may extend to other viruses with similar structural and immunological properties.

My expertise lies in the structural determination of antibody-antigen complexes in influenza and other pathogens. While I may not have sufficient expertise to evaluate specific technical details of the fluorescence-based methods employed, the authors have convincingly demonstrated the robustness of their experimental design and interpretation, supported by appropriate controls.

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

SUMMARY In "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", Benegal et al. develop a microscopy-based assay to measure dissociation of HA head-binding antibodies from intact virions. This assay allows the authors to explore the contribution of IgG bivalent avidity to antibody interaction with native virions, which is not accessible using other methods such as BLI. Using this assay, the authors further explore the effect of HA density on IgG avidity with engineered low-HA virions and then with artificial HA-coated microspheres. In addition to measuring antibody dissociation, the authors perform structural analyses to predict the conformational preferences of many HA IgGs from published structures. The authors conclude that low HA densities (down to ~10%) still support high avidity binding for the 2 IgGs tested, and thus there would be little evolutionary pressure for IAV to reduce the HA density as a strategy to evade immune recognition.

MAJOR COMMENTS

The data presented are generally convincing for the two antibodies tested, with some caveats listed below. I believe the microscopy technique is valuable and provides a significant contribution to the field, and I believe that the finding that avidity persists at low densities for IAV is compelling and worth communicating to other virologists. Overall, with the incorporation of the suggested major revisions, this manuscript represents a significant advancement in the field.

A major limitation of the current study is the small number of antibodies tested. Two antibodies are quite few, particularly since this work attempts to generalize these observations with structural predictions of dozens or hundreds of HA antibodies. While I believe that the resilience of IgG binding to lower epitope densities is likely common to many HA antibodies (or antibodies in general), this work alone does not support this. To this end, the authors should acknowledge their limited sample size in the text or discussion and that the generalization to other antibodies is speculative. Alternatively, the authors could demonstrate with additional antibodies (such as F045-092 which is pointed out in Fig S3A and perhaps group 'i' antibodies according to Fig S3A).

This is an important point, and we more explicitly acknowledge this limitation in lines 277-278.

It seems to me lateral diffusion of HA in the viral membrane is an important discussion point that was missed in this manuscript. The authors should comment on what is known about the lateral mobility of HA on virions, and how this could impact the ability of an IgG to crosslink. The authors should comment about whether long range diffusion and/or short range "shuffling" of glycoproteins could contribute to crosslinking preferences of antibodies in addition to the tilt, which is the only movement discussed. As appropriate, the authors should then comment on how this may affect their interpretation of experiments using beads. In experiments on beads, there is certainly no lateral mobility of the HA trimers; what are the consequences of this on the analysis?

We agree that this is an important consideration, and we have revised the manuscript (lines 296-298) to address these points. Briefly, we have previously performed fluorescence recovery after photobleaching of covalently labeled HA and NA on the surface of filamentous influenza particles (10.7554/eLife.43764; see Figure 1B of this reference for a representative example). This data indicates that long range diffusion does not seem to be occurring on the virion surface. Short range diffusion, or shuffling, has not been observed, but cannot be ruled out, and may increase conformations favorable to bivalent binding.

Should the authors qualify the limitations in the scope of their experimental results and the system of choice (beads vs. virions) as described in my previous comments, I suggest three experiments that I believe are essential to support the authors' claims. Alternative to qualifying the limitations, two optional experiments are also listed that could support the authors' claims as they are - those require a more extensive experimental undertaking and are thus labeled [OPTIONAL].

1) The photobleaching experiment shown in Figure S1A. I am concerned that measuring photobleaching in steady state conditions does not properly control for the experimental conditions. In steady state, bleached antibody could unbind and be replaced by fluorescent antibody that has diffused into the field of view. This should be more thoroughly controlled by irreversibly capturing antibody (such as with biotin) and imaging after excess antibody is washed away, or by some other method such as capturing and imaging virus that has been directly labeled with AF555. This should be possible using reagents and techniques already demonstrated by the authors.

We have updated the supplemental information with a more rigorous control for photobleaching; the revised figures are shown in Fig S1A. In this experiment, fluorescent S139/1 IgG was bound to HK68 virions. The antibody was washed away, and the loss of fluorescence signal was imaged separately under two conditions: 1) Dissociation only; an image was collected at 0s and one at 60s. 2) Dissociation and photobleaching; an image was collected at a rate of 1 frame per second for 60 seconds. The difference between the endpoint intensities from both conditions is not statistically significant. This supports our conclusion that, in the absence of antibodies in solution that can exchange with those bound to virions, photobleaching does not make a detectable contribution to the loss of signal we observe in our antibody dissociation experiments.

2) In imaging, the authors analyzed only filamentous virions because they exhibit the best signal to noise ratio, which is a reasonable technical simplification. However, this relies on the assumption that glycoprotein presentation is relatively constant between virions of different sizes. It would be helpful to perform some analysis of small virions in any movie where there is sufficient signal. This would support the assumption that rates for small virions are comparable to those of filaments in the same experiment. This should be possible by performing additional analysis on existing data, without requiring additional experiments.

Thank you for calling our attention to a point that needs clarification. The analysis that was restricted to filaments was for the SEP-HA binding experiments (shown in Fig 3A&B). This was done in order to select only those particles that were not diffraction-limited, so that we could control for any systematic differences in size between the two populations by measuring HA signal per unit particle length. For the dissociation experiments (Fig 2), data was taken from all virions in the fields of view. For this analysis, the normalized dissociation curves were averaged in two ways to account for the potential discrepancy that the reviewer points out. In the first method, the average was taken with each virion equally weighted, while in the second method, the entire field of view was masked and normalized together. Both curves look very similar, suggesting that any potential differences between smaller virions and filaments are not enough to make a quantifiable difference in dissociation rate. A representative dissociation curve with both analyses shown side-by-side has been added in Figure S1B.

3) In figure 3, C05 fab binding is used to assay HA content of the SEP HA virions. An additional method of confirming HA content that is more independent from the imaging assay would be beneficial, such as a Western blot to quantify HA relative to NP, NA, or M1 etc.

We have used western blotting to quantify the amount of HA contained relative to M1 in each population. This new data is discussed in lines 163-168 of the revised manuscript and shown in Figure S2C. As noted in the revised text, western blot analysis suggests that the density of native HA is decreased to ~31% its normal level in SEP-HA virions, lower than the ~75% value determined via fluorescence microscopy. One possible reason for this disparity is the presence of virus-like particles in the SEP-HA sample that completely lack wildtype HA. These would be excluded from our imaging analysis but captured by the western blot.

4) [OPTIONAL] In figure 4, it is depicted that FISW84 biases HA in a tilted conformation, and the authors reasonably propose the reduced flexibility discourages crosslinking by IgGs. From the modeling summarized in Figure S3A, are there any antibodies predicted to prefer crosslinking HA at the same angle FISW84 tilts the ectodomain? Would FISW84 enhance crosslinking by such an antibody?

This is an interesting suggestion, and we have revised the manuscript (lines 247-249) to clarify our thinking on this point. Based on the structure of the FISW84 Fab (PDB ID 6HJQ), we conclude that binding of a single Fab fragment does not necessarily actively tilt the HA ectodomain in a specific direction. Rather, it restricts tilting in the direction that would cause a steric clash between the Fab and the membrane. As a result, HA can still sample a range of angles, but this range is no longer symmetrical about the ectodomain axis. By reducing the likelihood that two HA ectodomains would tilt towards each other at a favorable angle, we would expect all antibodies to be disadvantaged to some degree. A possible exception could be if three FISW84 Fab fragments manage to bind to a single HA trimer. In this case, the HA ectodomain would be forced to remain perpendicular to the membrane to accommodate them all. This would favor antibodies that prefer binding to HAs where the ectodomains are parallel to each other. In our analysis in Figure S3A, this includes primarily antibodies that bind to the HA central stalk, such as 31.b.09. However, we note that these antibodies may encounter barriers to bivalent binding that we do not consider here, including proximity to the FISW84 epitope and the high density of HA in the membrane.

5) [OPTIONAL] In figure S3A, the authors display theoretical tilt and spacing preferences for many HA antibodies based on published structures. Interestingly, their group iii antibody is predicted to prefer greater spacing and tilt, and likewise the authors observe increased binding at lower densities (in figure 3E). It would be beneficial to the work to test group i antibodies (base binding) in the dissociation experiments. The behavior of a base binding antibody, particularly at low densities could reinforce the modeling performed for this work.

This is an excellent suggestion which we are not currently able to pursue for technical reasons. In particular, it would be difficult to distinguish between increased binding of these antibodies at low antigen densities that is due to bivalent attachment (and thus reduced dissociation) versus increased accessibility of the epitope, which may be occluded at higher HA densities.

The experiments are well explained and supported by methods that would enable reproducibility.

The authors state "The statistical tests and the number of replicates used in specific cases are described in the figure legends" yet in many cases this information is absent. For the k values in fig 2D, some indication of error or confidence interval would be helpful.

We have ensured that this information is included in each of the captions. Regarding the k values, formal error propagation is challenging due to the way the k values were derived. Specifically, these values were calculated by fitting the average of the three initial dissociation traces, rather than fitting each replicate individually and then averaging the rate constants. As a result, the usual methods for estimating confidence intervals or standard error of the mean are not directly applicable.

MINOR COMMENTS

o Some of the small details in fig 1A and fig S1 are lost due to small figure size - such as the sialic acid residues and lipid bilayer.

We have resized the figure components.

o Although described in the text, it could be helpful to incorporate into figure 2 why the BLI data is shown for S129 fab. Perhaps indicate in 2C that that curve is "too fast to accurately measure" and perhaps near the table in 2D indicate the blue data is from Lee et al. It may be fine to simply remove the BLI results from the figure and refer to them only in the discussion of the experiments. Even with the measured data, the difference between fab and IgG is striking enough to support the paper, and the BLI data may be more confusing in the figure than it adds.

We have updated the caption for Figure 2D to clarify that binding between the S139/1 Fab and A/WSN/1933 HA is approaching the limit of detection in our assay, and that the additional rates are from Lee et al. We have also updated the table to make the presentation of the kinetic parameters more clear.

o In figure 3A, better describe the fluorescent components in the fluorescent images in the legend.

We have updated the caption for Figure 3A to describe the fluorescent components shown in the image. Specifically, the panel labeled 'HA' shows signal from a fluorescent FI6v3 scFv, while the panel labeled 'decoy' shows signal from the SEP-HA construct.

o From personal experience, the flexibility of HA ectodomain can be significantly affected by how much of the membrane proximal linker region is retained or removed. Could the authors comment on how they chose the cutoff for their HA ectodomain used in the bead experiments and their rationale?

This is an important point, and while the precise impact of the linker on HA flexibility remains uncertain, we agree that it may increase the freedom of motion of the ectodomain relative to the HA membrane anchor. We mention this caveat in the revised text (lines 188-191) and we have added an AlphaFold2 prediction of how our recombinant HA might look to Figure S2D.

o In Figure S1B, if I understand correctly: black dashed line "IgG equivalent dissociation rate" is the experimental data, magenta "Crosslinking model fit" is the theoretically total antibody bound as described by the mathematical model. Then the gray lines "Double- /singly- bound antibodies plot the theoretical amount of antibody bound once and bound twice. If this is correct, I believe it would be clearer if the singly- and doubly- bound were plotted in separate colors, and that this is explained more clearly in the legend.

We have revised the figure to show doubly- and singly-bound curves using different line styles.

o Related to an earlier comment, if lateral diffusion may play a role, how might this differ between different types of antibodies?

As mentioned in our previous response, we do not anticipate that lateral diffusion makes a significant contribution to antibody binding to the surface of virions, although it may be important on the cell surface.

o Could the authors comment in the discussion on how their results on virions may translate to the surface of the infected cell, which is also decorated in viral glycoproteins? Early time points of infection could be an in vivo example of low-density HA. What extent may antibody binding and crosslinking affect viral proteins on the cell surface or the immune response?

This is a very interesting point. Antibody binding to the infected cell surface has been shown to alter viral release and morphology, presumably at lower HA densities than those observed the viral surface. We have added a brief discussion of this point (lines 291-295) to the revised manuscript.

o The github link in the methods is incorrect or not yet available.

Thank you for noting this. We have updated the link.

o Reference 1 has an incorrect or expired link.

These references have been updated.

Reviewer #3 (Significance (Required)):

• This work represents a conceptual advance in our understanding of antibody action on viral pathogens. The authors adapt existing microscopy methodologies to measure antibody avidity in a new way that is better representative of in vivo conditions.

• To my knowledge, this is the first instance of direct measurement of antibody off-rates from intact virus particles, instead of immobilized protein as in BLI, SPR, or interferometry.

• This work should be of interest to virologist and biophysicists interested in the cooperative binding of antibodies and the relation of virus structural organization to antibody recognition. Immunologist may also be influenced by this work. This work may be followed up by other researchers similarly measuring the association and dissociation rates of antibodies with single virions, or otherwise comparing fab to IgG binding to gain insight into when crosslinking is or is not occurring.

• Reviewer expertise: Single-virion imaging, protein complexes, biochemistry, influenza A.

• I do not have sufficient expertise to evaluate the mathematical models and differential equations for modeling the k-on and k-off rates.

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Referee #3

Evidence, reproducibility and clarity

Summary

In "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", Benegal et al. develop a microscopy-based assay to measure dissociation of HA head-binding antibodies from intact virions. This assay allows the authors to explore the contribution of IgG bivalent avidity to antibody interaction with native virions, which is not accessible using other methods such as BLI. Using this assay, the authors further explore the effect of HA density on IgG avidity with engineered low-HA virions and then with artificial HA-coated microspheres. In addition to measuring antibody dissociation, the authors perform structural analyses to predict the conformational preferences of many HA IgGs from published structures. The authors conclude that low HA densities (down to ~10%) still support high avidity binding for the 2 IgGs tested, and thus there would be little evolutionary pressure for IAV to reduce the HA density as a strategy to evade immune recognition.

Major comments

The data presented are generally convincing for the two antibodies tested, with some caveats listed below. I believe the microscopy technique is valuable and provides a significant contribution to the field, and I believe that the finding that avidity persists at low densities for IAV is compelling and worth communicating to other virologists. Overall, with the incorporation of the suggested major revisions, this manuscript represents a significant advancement in the field.

A major limitation of the current study is the small number of antibodies tested. Two antibodies are quite few, particularly since this work attempts to generalize these observations with structural predictions of dozens or hundreds of HA antibodies. While I believe that the resilience of IgG binding to lower epitope densities is likely common to many HA antibodies (or antibodies in general), this work alone does not support this. To this end, the authors should acknowledge their limited sample size in the text or discussion and that the generalization to other antibodies is speculative.

Alternatively, the authors could demonstrate with additional antibodies (such as F045-092 which is pointed out in Fig S3A and perhaps group 'i' antibodies according to Fig S3A).

It seems to me lateral diffusion of HA in the viral membrane is an important discussion point that was missed in this manuscript. The authors should comment on what is known about the lateral mobility of HA on virions, and how this could impact the ability of an IgG to crosslink. The authors should comment about whether long range diffusion and/or short range "shuffling" of glycoproteins could contribute to crosslinking preferences of antibodies in addition to the tilt, which is the only movement discussed. As appropriate, the authors should then comment on how this may affect their interpretation of experiments using beads. In experiments on beads, there is certainly no lateral mobility of the HA trimers; what are the consequences of this on the analysis?

Should the authors qualify the limitations in the scope of their experimental results and the system of choice (beads vs. virions) as described in my previous comments, I suggest three experiments that I believe are essential to support the authors' claims. Alternative to qualifying the limitations, two optional experiments are also listed that could support the authors' claims as they are - those require a more extensive experimental undertaking and are thus labeled [OPTIONAL].

1. The photobleaching experiment shown in Figure S1A. I am concerned that measuring photobleaching in steady state conditions does not properly control for the experimental conditions. In steady state, bleached antibody could unbind and be replaced by fluorescent antibody that has diffused into the field of view. This should be more thoroughly controlled by irreversibly capturing antibody (such as with biotin) and imaging after excess antibody is washed away, or by some other method such as capturing and imaging virus that has been directly labeled with AF555. This should be possible using reagents and techniques already demonstrated by the authors.
2. In imaging, the authors analyzed only filamentous virions because they exhibit the best signal to noise ratio, which is a reasonable technical simplification. However, this relies on the assumption that glycoprotein presentation is relatively constant between virions of different sizes. It would be helpful to perform some analysis of small virions in any movie where there is sufficient signal. This would support the assumption that rates for small virions are comparable to those of filaments in the same experiment. This should be possible by performing additional analysis on existing data, without requiring additional experiments.
3. In figure 3, C05 fab binding is used to assay HA content of the SEP HA virions. An additional method of confirming HA content that is more independent from the imaging assay would be beneficial, such as a Western blot to quantify HA relative to NP, NA, or M1 etc.
4. [OPTIONAL] In figure 4, it is depicted that FISW84 biases HA in a tilted conformation, and the authors reasonably propose the reduced flexibility discourages crosslinking by IgGs. From the modeling summarized in Figure S3A, are there any antibodies predicted to prefer crosslinking HA at the same angle FISW84 tilts the ectodomain? Would FISW84 enhance crosslinking by such an antibody?
5. [OPTIONAL] In figure S3A, the authors display theoretical tilt and spacing preferences for many HA antibodies based on published structures. Interestingly, their group iii antibody is predicted to prefer greater spacing and tilt, and likewise the authors observe increased binding at lower densities (in figure 3E). It would be beneficial to the work to test group i antibodies (base binding) in the dissociation experiments. The behavior of a base binding antibody, particularly at low densities could reinforce the modeling performed for this work.

The experiments are well explained and supported by methods that would enable reproducibility.

The authors state "The statistical tests and the number of replicates used in specific cases are described in the figure legends" yet in many cases this information is absent. For the k values in fig 2D, some indication of error or confidence interval would be helpful.

Minor Comments

• Some of the small details in fig 1A and fig S1 are lost due to small figure size - such as the sialic acid residues and lipid bilayer.
• Although described in the text, it could be helpful to incorporate into figure 2 why the BLI data is shown for S129 fab. Perhaps indicate in 2C that that curve is "too fast to accurately measure" and perhaps near the table in 2D indicate the blue data is from Lee et al. It may be fine to simply remove the BLI results from the figure and refer to them only in the discussion of the experiments. Even with the measured data, the difference between fab and IgG is striking enough to support the paper, and the BLI data may be more confusing in the figure than it adds.
• In figure 3A, better describe the fluorescent components in the fluorescent images in the legend.
• From personal experience, the flexibility of HA ectodomain can be significantly affected by how much of the membrane proximal linker region is retained or removed. Could the authors comment on how they chose the cutoff for their HA ectodomain used in the bead experiments and their rationale?
• In Figure S1B, if I understand correctly: black dashed line "IgG equivalent dissociation rate" is the experimental data, magenta "Crosslinking model fit" is the theoretically total antibody bound as described by the mathematical model. Then the gray lines "Double-/singly- bound antibodies plot the theoretical amount of antibody bound once and bound twice. If this is correct, I believe it would be clearer if the singly- and doubly-bound were plotted in separate colors, and that this is explained more clearly in the legend.
• Related to an earlier comment, if lateral diffusion may play a role, how might this differ between different types of antibodies?
• Could the authors comment in the discussion on how their results on virions may translate to the surface of the infected cell, which is also decorated in viral glycoproteins? Early time points of infection could be an in vivo example of low-density HA. What extent may antibody binding and crosslinking affect viral proteins on the cell surface or the immune response?
• The github link in the methods is incorrect or not yet available.
• Reference 1 has an incorrect or expired link.

Significance

• This work represents a conceptual advance in our understanding of antibody action on viral pathogens. The authors adapt existing microscopy methodologies to measure antibody avidity in a new way that is better representative of in vivo conditions.
• To my knowledge, this is the first instance of direct measurement of antibody off-rates from intact virus particles, instead of immobilized protein as in BLI, SPR, or interferometry.
• This work should be of interest to virologist and biophysicists interested in the cooperative binding of antibodies and the relation of virus structural organization to antibody recognition. Immunologist may also be influenced by this work. This work may be followed up by other researchers similarly measuring the association and dissociation rates of antibodies with single virions, or otherwise comparing fab to IgG binding to gain insight into when crosslinking is or is not occurring.
• Reviewer expertise: Single-virion imaging, protein complexes, biochemistry, influenza A.
• I do not have sufficient expertise to evaluate the mathematical models and differential equations for modeling the k-on and k-off rates.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this study, Benegal et al. investigate the binding kinetics of HA-head-specific antibodies (S139/1 and C05) to intact influenza virus particles using a fluorescence microscopy-based technique to measure the dissociation rate (koff) of the antibodies. By applying their proposed equilibrium model for bivalent antibody binding to HA, the authors calculated the crosslinking rate (kx), which represents the rate at which a single-bound antibody crosslinks to an additional HA molecule. Their experiments revealed that antigen crosslinking significantly slows koff, reducing it by up to two orders of magnitude.

The authors further utilized streptavidin-coated beads conjugated with biotinylated HA or biotinylated BSA at varying concentrations to control HA surface density. Their results demonstrated that the two tested HA-head-specific antibodies retained the ability to crosslink HAs even at ~10-fold lower HA surface densities. In a complementary experiment, they employed an HA-anchor-specific antibody to restrict HA flexibility, which led to reduced binding of S139/1 and C05 IgGs but not their Fab fragments. This finding suggests that HA flexibility, rather than density, is the primary determinant of antibody crosslinking and avidity.

Overall, the authors present an innovative approach to elucidating the dissociation and crosslinking kinetics of antibodies targeting intact virions or nanoparticles. The study is well-designed, with alternative interpretations of the results carefully considered and addressed throughout. I have only a few minor comments and suggestions for clarification.

Minor comments:

1. In Figure 1, does the grey color of each IgG in panel C indicate the Fc domain? If so, please add the description of the colors to the figure legend. In fact, it may be better to explain all the colors used here (for HA1, HA2, Fab heavy chain, light chain, etc.).
2. Under the section," Bivalent binding of S139/1 and C05 persists after ~10-fold reductions in HA surface densities", the beginning of the second paragraph writes, "For both S139/1 and C05 Fab, binding increases linearly with HA density, as expected for a monovalent interaction dictated by absolute HA availability rather than density (Fig. 3D). Interestingly, the same relationship is observed for S139/1 IgG."

Visually, I think the same relationship also seems to hold for C05 IgG. Would it be better to perform some linear regression and report the R2 value for the fitting so that this assessment can be quantitative? 3. At the end of the same page, in the same paragraph, the authors mentioned, "In contrast to the IgG, Fab binding measured at twice the molar concentration of the IgG is nearly undetectable under these conditions, confirming the IgG binding is not occurring through monovalent interactions (Fig. S2E)." What are the conditions you are referring to? In Fig. S2E, there is only the Ab intensity for the Ab binding at 100% HA (and not the other percentages). For the Ab intensity of S139/1 Fab, what is the concentration of the Fab used in Figure 3D? Why could the intensity in this experiment for S139/1 Fab reach ~100,000, whereas that of the 8 nM in Fig. S2E can only reach ~20,000? 4. Under the section, "Tilting of HA about its membrane anchor contributes to C05 and S139/1 avidity", in the second paragraph, the authors wrote, "If this is correct, we reasoned that avidity could be reduced by constraining tilting of the HA ectodomain. To test this hypothesis, we used FISW84, an antibody that binds to the HA anchor epitope and biases the ectodomain into a tilted conformation (Fig. 4B)."

Can you use some computational models (maybe the same one you used for Figure 4A) to show that when an HA trimer is bounded by FISW84 Fabs, the tilting of HA is constrained? I think this will help substantiate the assertion above. 5. It would be good if you could mention the strain of HA used in the experiments in Figure 4 in the actual Figure as well (as supposed to just in the figure legend). 6. I do not see a method section for the structure-based model you used in Figure 4. In the text, you cited your previous study (ref 28) for the model, but it would be good to write about this briefly (and how you specifically apply the model in this study) in this current manuscript. 7. In Figure S1 panel D, what is the unit of the antibody concentration? Could you please add it to the graph legend?

Significance

Previously, this group utilized the same fluorescence-based method to investigate the potency of anti-HA IgG1 antibodies in preventing viral entry versus egress, as well as the tendency of antibodies targeting different HA epitopes to crosslink two HA trimers in cis or in trans (He et al., J Virol, 2024). In this study, they extend their work by evaluating, in-depth, how the density and flexibility of hemagglutinin (HA) on the viral surface influence the binding avidity of anti-HA antibodies. Using two human IgG1 antibodies targeting the HA head, the authors demonstrate that these antibodies can crosslink two HA trimers in cis, even when the trimers are further apart than adjacent HAs. Notably, the study reveals that HA flexibility, rather than density, is the key determinant modulating antibody crosslinking. Even at a 10-fold reduced HA density compared to the original, the antibodies retained their ability to crosslink trimers.

This study provides critical insights into the relationship between HA density, flexibility, and antibody function, adding to the broader understanding of antibody crosslinking-a topic frequently discussed in the field of influenza research. These findings could have significant implications for vaccine design, particularly for strategies involving the display of the HA ectodomain on nanoparticles, potentially guiding the development of more effective influenza vaccines. Furthermore, the broader relevance of these findings may extend to other viruses with similar structural and immunological properties.

My expertise lies in the structural determination of antibody-antigen complexes in influenza and other pathogens. While I may not have sufficient expertise to evaluate specific technical details of the fluorescence-based methods employed, the authors have convincingly demonstrated the robustness of their experimental design and interpretation, supported by appropriate controls.

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Referee #1

Evidence, reproducibility and clarity

Comments for the authors of Review Commons Manuscript RC-2024-02804:

The author of the Review Commons manuscript "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", present their recent work evaluating hemagglutinin interactions with cellular receptors and antibodies. This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Thie findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies. Below are some comments that I would like the authors to address as they revise the manuscript.

Comments:

1. Can the authors provide justification for the two influenza viruses that they used.
2. The use of filamentous particles is a strength, but authors should detail the role of filamentous vs. spherical in nature and lab settings. This will help researchers that plan to repeat these assays.
3. Did the authors add the Udorn M1 to the HK68 as well?

Significance

This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Thie findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies.

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Reply to the reviewers

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

In Morris, M.J. et al., the authors strive to better understand the roles for the microcephaly protein WDR62 in brain growth and function. To accomplish this, an in situ biotinylation assay was performed and identified 42 proteins proximal to WDR62 including the Hsp70 co-chaperone BAG2. Through a series of co-immunoprecipitation assays, the BAG2-WDR62 interaction was shown to be mediated through the structured N-terminal region of WDR62, and it was proposed that common WDR62 mutations disrupt this interaction. In AD293 cells, loss of WRD62 expression resulted in an increase in the expression of BAG2 expression while reducing HPRT expression. Subsequent loss of BAG2 expression by siRNA treatment restored the expression of HPRT suggesting that there is an association between the stability of HPRT and BAG2, likely mediated through its proposed association with Hsp70/90 molecular chaperones. Finally, the authors investigate the subcellular localization and ability of WRD62 to phase separate. WRD62 was shown to form discrete condensates induced by sorbitol-mediated hyperosmotic stress. The formation of WRD62 granules are hypothesized to be driven by cell volume exclusion and macromolecular crowding. These granules appear similar, both in physical appearance and characteristics, to other reported biomolecular condensates such as those reported in metabolism (e.g. purinosomes). WRD62-containing condensates were shown to colocalize with enzymes in de novo purine biosynthesis; however, this association is not required for purinosome formation and/or its stability under both purine-depleted and sorbitol-driven growth conditions. Overall, the manuscript provided a previously unrealized and exciting association between WDR62 and purine metabolism.

EVIDENCE, REPRODUCIBILITY AND CLARITY Summary: The current manuscript reads as multiple manuscripts with findings that are at times weakly connected (in my opinion). For example, I had a hard time understanding how the BioID results relate to the discovery of WRD62 phase-separation and its colocalization with purinosomes. I would strongly encourage the authors to consider dividing the results into separate manuscripts to strengthen their claims and create a more focused and cohesive manuscript (or series of manuscripts). I believe then several of my reservations associated with the current manuscript will be addressed, and in my opinion, the hard work from the authors will be better received across the scientific community.

Response: We thank Reviewer #1 for acknowledging the novelty of our work and appreciate the constructive feedback regarding the lack of integration among individual findings. In response, we have removed content related to condensate formation and conducted additional experiments to more thoroughly characterize the mechanisms of WDR62 interaction. These new data, along with revisions to the manuscript text, have strengthened the coherence of our findings. We believe the revised manuscript now presents a more unified narrative, highlighting the complex roles of WDR62 in regulating purine metabolism.

I would like to commend the authors for all the work that went into the current version of the manuscript. Being part of a biochemistry and cell biology research group, I completely understand how much time and effort must have went into generating these data. That being said, I felt that there were several instances where clarification and additional information is warranted to arrive at the conclusions made by the authors. These points are outlined below.

Major Comments:

1. There appears to be a discrepancy between the data presented in Figure 1 and what is stated in the main text. Clarification is necessary to better understand the results:

• The following statement (and derivatives of it) are repeated throughout the manuscript: "...we found that the WDR62 interactome comprised molecular chaperones such as HSP70, HSP90, and their co-regulators, BAG2, STIP1, and DNAJC7" (lines 91-93, 316-318, 422-425). STIP1 and DNAJC7 were not identified in the list of 42 proximal proteins to WDR62 (Figure 1D). DNAJC7 was included because of a previous report curated in the BioGRID database, and there is no mention of HSP90 in the data produced in Figure 1. Please revise the main text to reflect the data that was generated.

Response: We thank the reviewer for this valid point and highlighting the instances where our description of results did not accurately reflect the data generated. We have reworded the relevant sections (e.g. lines 105-107) in our revised manuscript to better delineate interactors identified in BioID studies (BAG2) as opposed to those previously reported on protein interaction databases such as BioGRID (DNAJC7).

Based on the data presented in the Venn Diagrams in Figure 1D, the author's numbers do not seem to be consistent with the sentence on lines 126-128. I count 37 proteins unique to their BioID study, 90 unique to the BioGRID database, and 5 proteins that overlap between the two data sets. This sentence needs to be revised.

Response: We thank the reviewer for pointing out this inconsistency. There were 95 protein interactors of WDR62 from BioGRID while we identified 42 proteins in our BioID study with 5 proteins overlapping. We have revised the main text (lines 144-146) and Fig. 1D to accurately reflect the protein numbers identified.

What data were used to generate the interaction map in Figure 1I? Enzymes tied to purine metabolism were not identified from the data presented in Figure 1D but have now appeared. A discussion of this in the main text is warranted.

Response: We generated the interaction map in Fig. 1I using STRING to visualise WDR62 protein-protein interactions derived from both the BioGRID database and our BioID analysis. As the reviewer correctly points out, purine metabolic enzymes were not direct interactors of WDR62. Purine enzymes are linked to the molecular chaperones which, in turn, associated with WDR62 from our BioID analysis. The links between purine enzymes and chaperones were obtained from the BioGRID database. In response to this feedback, we have revised our manuscript to include a more detailed description of how the interaction map in Fig. 1I was generated, both in the main text (lines 148-157) and the legend for Figure 1. The BioGRID interactions between heat shock proteins and purine enzymes were introduced in the manuscript text at lines 264-266.

1. This reviewer has several reservations on how the various key players in the manuscript are related to substantiate the conclusions made in the manuscript. For instance, how is HPRT, purinosomes, and WDR62 related? How about HSP90, WRD62, and HPRT? Pairwise connections were made throughout the manuscript; however, trying to tie all three together is difficult with the data presented.

• The authors tried to connect HPRT, purinosomes, and WDR62 with BAG2; however, this study could greatly improve if we understood how a knockdown of BAG2 impacts purinosome formation and/or WDR62 colocalization with purinosome enzymes.

Response: We have incorporated additional experiments in our revised manuscript to better connect HPRT, WDR62 and BAG2. Using proximity ligation assays (PLA) we demonstrated endogenous interactions between WDR62 and BAG2 (Fig. 4K), as well as between WDR62/HPRT and BAG2/HPRT (Fig. 6I-J). The interaction between BAG2 and HPRT was decreased in WDR62 KO cells (Fig. 6J), and recent experiments revealed that BAG2 depletion similarly disrupted the WDR62/HPRT interaction. These findings suggest that WDR62 expression, and presumably its interaction with BAG2, is necessary for BAG2-mediated regulation of HPRT.

Further, we found that the loss of HPRT expression in WDR62 KO cells was reversed by siRNA depletion of BAG2 (Fig. 6K), supporting our model in which elevated BAG2 levels in the absence of WDR62 promote aberrant HPRT degradation. Collectively, our results suggest that proper BAG2 regulation of HPRT requires WDR62.

To address the reviewer’s suggestion, we also examined WDR62 cytoplasmic localisation following BAG2 depletion and found that BAG2 was not required for WDR62 to form granules in response to osmotic stress. We also show that BAG2 is not responsible for purinosome assembly or for the subcellular distribution/localisation of HPRT.

Is HPRT a client of HSP90? And how are WRD62 and HSP90 related since they do not associated (based on your BioID data)? These connections would again strengthen the arguments made in the manuscript and help to explain the HSP90 inhibition data presented in Figures 7F and 7G.

Response: Although our BioID data did not explicitly identify an association between WDR62 and HSP90, we initially focused on HSP90 due to the established role of BAG2 in protein misfolding and degradation through its interaction with HSP90 (doi: 10.7150/thno.78492). We hypothesised that while WDR62 may not directly interact with HSP90, its interaction with BAG2 could provide an indirect link. To strengthen our conclusions and address the limitations of our HSP90 inhibition data (NVP-AUY922), we performed additional experiments using a second HSP90 inhibitor (17-AAG) and an HSP70 inhibitor (MKT-077) across both short (1 h) and long (24 h) treatment durations (Fig 6 and Fig S10). Further details are provided in our response below to minor comment #1.

Caution is warranted when making conclusions about WDR62 (and its granules) and purinosomes.

Response: We acknowledge the reviewer’s feedback and have revised our manuscript to focus on the functional characterisation of WDR62 interaction and co-localisation with BAG2 and related HSP co-chaperones. As part of this revision, we removed the FRAP studies and sections discussing WDR62 phase separation and purinosome assembly (further details below). Additionally, we have softened out description of cytoplasmic WDR62 granules as purinosomes. Instead, we describe WDR62 as forming dynamic puncta containing purine enzymes and discuss the possibility that these granules may represent or overlap with bona fide purinosomes.

The authors describe the association between WDR62 and purinosomes differently throughout the text. I would recommend that the authors come to some conclusion about this and be consistent.

Response: We thank reviewer #1 for pointing out inconsistencies in our conclusions regarding WDR62 and purinosomes between sections of our manuscript. We have revised our manuscript to ensure our description of these findings are consistent throughout. Specifically, our findings show that WDR62 responds to osmotic and metabolic stress by forming dynamic cytoplasmic granules that share many protein components with purinosomes (Fig. 5). This suggests that WDR62 may be a novel component of bona fide purinosomes or that WDR62 granules substantially overlap with purinosomes both spatially and compositionally. However, the formation of granules by purine enzymes was not perturbed by WDR62 KO (Fig. S6). Thus, we conclude that while WDR62 colocalized with purine enzyme containing granules consistent with purinosomes in response to cell stress, WDR62 was not required for granule formation by purine enzymes such as PFAS and PPAT.

A. (Lines 339-340) "WDR62 granules represent or overlap substantially with the phase-separated metabolons known as purinosomes". Based on the data presented, it appears that these might still be different entities but either overlap or have similar components. Purinosome localization with mitochondria (approx 60-80%) and microtubules (approx 90-95%) were significantly higher than those reported for WDR62 granules (approx 40%). This comparison would suggest that not all WDR62 granules behave similarly to purinosomes. And from the dot plot in Figure 3G, about half of the characterized WDR62 granules do not align with the previously reported characteristics of purinosomes.

Response: In Fig. 3G, we measured the diameter and distribution of WDR62 granules and found their size and number per cell closely matched those reported for BAG2 condensates (doi: 10.1038/s41467-022-30751-4). This aligns with our findings that WDR62 interacts with BAG2 and is recruited to similar subcellular compartments. The reviewer correctly notes that WDR62 granules only partially align with previously reported characteristics of purinosomes, suggesting that they may be distinct entities. Our revised manuscript acknowledges this possibility while also emphasising that WDR62 granules share features and colocalise with many purinosome components. To enhance the focus and clarity of the manuscript, we have removed Fig. 3G as the diameter and number of WDR62 granules are already reported in Fig. 3F.

In the abstract and introduction, the authors state that WDR62 is being recruited to the purinosome and leave out the other possibility. I would recommend that the authors soften this claim in these sections because of the above possibility but also the lack of characterization of the sorbitol-induced "purinosomes". There is little discussion or evidence for how sorbitol induces purinosome formation. Is de novo purine biosynthesis activated upon sorbitol treatment? Are multiple de novo purine biosynthetic enzymes present in the sorbitol-induced "purinosomes"? Further, I agree that there is a tendency for WDR62 to associate with condensates that bear an enzyme within de novo purine biosynthesis; however many of these proteins are known to self-aggregate upon cell stress. Therefore, the entities that are being observing and called purinosomes might not be bone fide purinosomes. Additional care is necessary to make these statements. In my opinion, the current data only suggests that this might be a possibility.

Response: As indicated, we have softened our claim that stress-induced WDR62 granules represented bona fide purinosomes. Fig. 3 of our revision more precisely describes the characteristics of WDR62 granules while Fig. 4 now reports on the co-localisation of WDR62 granules with protein chaperones and de novo purine synthesis enzymes typically associated with purinosomes. We now conclude that WDR62 may be associated with purinosomes but may also represent distinct entities with shared components and characteristics. Notably, proteins such as BAG2 and PFAS may undergo phase separation in response to stress independently of purinosome assembly.

In additional work conducted for our revised manuscript, we find that WDR62 loss reduced rates of purine synthesis in cells cultured in the presence of purines (Fig. 5) but was not involved in de novo purine biosynthesis under purine-depleted conditions (Fig. S9). This was consistent with the finding that WDR62 loss did not prevent stress-induced formation of PFAS or PPAT granules (Fig. S6) which are likely to represent purinosomes. We concede that additional investigation is required to determine the functional significance of WDR62 granules in response to stress stimuli and purine depletion.

(Lines 325-329) The authors reference a previous manuscript demonstrating that co-chaperones co-cluster with purinosomes. Based on this fact, they infer that WDR62 granules might represent purinosomes since WDR62 interacts with these same set of co-chaperones. These co-chaperones interact with a large number of different proteins (in fact, most kinases), so it is uncertain how the authors decided to go down this path to link purine metabolism with WDR62. Discussion of how this connection was made would help elevate the story. What additional insights did they have that lead them down these investigations?

Response: BAG2 functions as a co-chaperone that regulates the activity of HSP70/90. While the reviewer correctly points out that co-chaperones such as BAG2 have a broad number of clients, numerous studies have established the role of HSP70/90 in purine metabolism (e.g. doi: 10.1016/j.isci.2020.101058, 10.1073/pnas.1300173110) and in neurodevelopment (10.3389/fnins.2018.00821). Moreover, purines are critical for normal brain development and dysregulation is well known to lead to congenital defects including microcephaly. As such, when we identified a role for WDR62 in the chaperone network through interaction with BAG2, it was not a leap to hypothesise that neurometabolic defects stemming from dysregulated purine production or salvage might be involved in WDR62-associated microcephaly.

Indeed, we show that WDR62 are localised with purine enzymes in response to purine-depletion and that WDR62 depletion leads to metabolic dysregulation. WDR62 has several binding partners with multiple cellular functions, and we do not exclude alternative mechanisms involved in cortical development. However, the mechanistic link with heat shock proteins and purine metabolism is a novel one that would be of broad interest in molecular neurodevelopmental biology. On this feedback, we have revised main text (lines 214-218, lines 260-263, lines 292-295, lines 378-383) to better explain the rationale underlying our experiments and overall study focus.

If WDR62 is not required for purinosome formation, why would it localize with the purinosome? Is there any hypothesis that could be readily tested to better help understand this observation? Providing a better understanding of this would greatly elevate the work.

Response: Given the role of HSP70/90 in purinosome assembly and the interaction of WDR62 with BAG2, and purine enzymes PFAS and PPAT, we were initially surprised that WDR62 depletion did not affect stress-induced PFAS and PPAT granule formation (Fig. S6). At the time of writing the original manuscript, we interpreted these granules as purinosomes. However, it remains possible that WDR62 might have a function in purine synthesis or in purinosome assembly that remains unidentified. Indeed, we have not yet tested different cell types or additional conditions that induce purinosome formation or determined the localisation or activity of other purine synthesis enzymes. Thus, we concede our conclusions on WDR62 and purinosome formation were premature.

As our revised manuscript is now focused on the WDR62-BAG2-HPRT interaction and given the reviewer’s prior comment that PFAS and PPAT colocalization in granules may not represent purinosomes in all contexts, we acknowledge that potential WDR62 functions in purinosomes warrants further investigation beyond this study. In the revised discussion (lines 473-497) we address these limitations and propose alternative interpretations of our findings.

(OPTIONAL) Please validate that the associations between WDR62 and the purine biosynthetic enzymes occur on the endogenous level (void of transient transfection). Many methods such as immunofluorescence and proximity ligation assays have been used by others to demonstrate protein-purinosome interactions. This result would reduce any concern that the association is a result of overexpression (artifact).

Response: As suggested, we conducted proximity ligation assays (PLA) to validate endogenous interactions between WDR62 and BAG2, HPRT, and PFAS (Fig. 4K, Fig. 6I-K). Notably, sorbitol treatment increased the interaction between WDR62 and HPRT (Fig. 6H, I), supporting the role of WDR62 in regulating HPRT under cellular stress. Additionally, WDR62 deletion appear to reduce the interaction between BAG2 and HPRT (Fig. 6K), while BAG2 depletion similarly reduces the interaction between WDR62 and HPRT (Fig. 6J). These findings support a model in which WDR62 and BAG2 cooperatively regulate HPRT stability.

Figures 6F and 6G conclude that nucleosides from purine-depleted growth conditions accumulate while the corresponding monophosphates do not change between WRD62 knock-out and wildtype cells. Given that purine-depleted growth conditions activate de novo purine biosynthesis (uncertain if this has been demonstrated in AD293 cells), could this result simply demonstrate that purine salvage is no longer used and the nucleosides have accumulated and are awaiting degradation (or exportation) rather than a loss of HPRT expression as inferred from the stated conclusions? The conclusions could be better substantiated with the use of a stable isotope incorporation assay.

Is there a difference in the contribution of de novo purine biosynthesis and purine salvage to the generation of the monophosphates (AMP, GMP) between WDR62 knockout and wildtype AD293 cells? Use of a stable isotope (such as 15N-glutamine) could help to come to the appropriate conclusion.

__Response: __We thank the reviewer for this helpful suggestion to better characterize WDR62-dependent purine defects in more detail. In our revised manuscript we performed targeted metabolomics experiments and tracked the incorporation of 13C2-glycine and 13C5-hypoxanthine into purine nucleosides to assess purine synthesis and purine salvage flux between WT and WDR62 KO cells (n=5). Indeed, purine nucleotides in KO cells showed a significant loss of incorporation of 13C2 from 13C2-glycine, consistent with impaired de novo synthesis in cells cultured in presence of purines. In contrast, labelling from 13C5-hypoxanthine showed no overt differences between WT and KO cells, suggesting that incorporation via the salvage pathway is not grossly altered under these conditions. We have subsequently added a section to the discussion (lines 498-521) to discuss these results which suggest that the reduced HPRT levels in KO cells may be sufficient to sustain rates of purine salvage which are not altered with WDR62 loss. Thus, the accumulation of nucleosides is most likely due to increase conversion from monophosphates or reduced degradation to uric acid. Nonetheless, we show that WDR62 is required for purine synthesis under basal conditions and has a complex role in regulating purine metabolism.

(Lines 483-485) If there is a change in de novo purine biosynthesis, are there any detectable changes in AICAR levels that might influence purine metabolism at the transcriptional level?

__Response: __This remains a possibility. However, we did not detect the AICAR intermediate in our untargeted LC-MS/MS metabolomics analysis perhaps due to low relative abundance and/or low stability. As a result, we were unable to comment on AICAR levels but this would be an interesting research direction to pursue in subsequent follow up studies.

Are the data and the methods presented in such a way that they can be reproduced? Are the experiments adequately replicated and statistical analysis adequate? 1. For purine-depleted studies (metabolite analyses, microscopy), how long were the cells grown in purine-depleted medium before the analysis? And how was the purine-depleted medium generated? Please reference any source that might have been used.

__Response: __We removed purines from the cell culture environment by incubating cells for 7 days with DMEM supplemented with FBS dialyzed to remove small molecules such as nucleosides and nucleobases. This important methodological detail was omitted in error in our original submission. Our revised manuscript includes description of how we depleted cells of purines in the Materials & Methods at Lines 636-640 with reference to source materials and prior studies.

Details describing the BioID experiment are minimal. How many replicates were performed, was label-free or TMT quantitation used for the protein identification. Further the data analysis and mining of the proteins from the BioID study are missing - What database was used to identify the proteins from the peptides? Please include this information in the Materials and Methods section as well as a link to a repository where the LC-MS/MS data generated can be found. Additionally, it would be very helpful to have a spreadsheet or table that lists the biotinylated proteins and expectant or p values for each.

__Response: __We performed three independent biological replicates (n = 3) for the BioID experiment. We apologise for the omission and have now included this information in the Fig. 1 legend. Label-free quantitation was used for protein identification, and peptides were identified using the ProteinPilot™ Software (v. 4.5) database. As part of our revision, we have updated the Materials and Methods section to include these details and will also provide a spreadsheet listing all biotinylated proteins across replicates, including their p-values. Furthermore, we have submitted our LC-MS/MS data as supplementary files associated with this manuscript.

Please include information about the streptavidin pulldown presented in Figure 1C.

__Response: __Streptavidin pulldown followed by immunoblot for known WDR62 interacting proteins is described in our Materials & Methods section at line 753-759. __ __Proteins bound to Streptavidin agarose beads were eluted with Laemmli buffer following washing. Pulldown fractions and total lysates were then resolved on SDS-PAGE, transferred to PVDF and blotted with primary antibodies to detect WDR62 interacting proteins such as CEP170, JNK and AURKA. We also used this method to confirm biotin-labelling and affinity isolation of BAG2 in Fig. 1C.

Many of the figure legends could benefit from a statistical description.

Response: As requested, we have updated the legends for all relevant figures and supplementary figures to include statistical descriptions, specifying analyses used and replicate (n) numbers. These additions complement the detailed description of our statistical methods provided in the Materials & Methods section (line 884).

There seems to be only two data points for Figure S3A. While there is no significant difference observed, it would be ideal to have additional replicates.

Response: We have completed an additional replicate and updated Fig. S3A for our revised submission. This study which now includes n = 3 independent biological replicates. While we observed a slight increase in the proportion of cells with MAPKBP1 granules in response to sorbitol stress, this change was not statistically significant. In contrast, WDR62 formed granules in a much larger proportion of cells (~90%) in response to stress (Fig. 3E).

(Figure 5I) Please provide statistical analysis to demonstrate the colocalization between FGAMS and WDR62 is robust in purine-depleted AD293 cells.

Response: Our revised manuscript now includes three independent replicates assessing WDR62 co-localisation with PFAS in purine-depleted AD293 cells (Fig. 4I in revision). We consistently observed a high degree of co-localisation, as quantified by Pearson’s correlation coefficient (mean = 0.8), which was significantly different from control conditions.

1. The use of HSP90 inhibitors is a little confusing given the connections being made with BAG2 and other HSP70 co-chaperones in Figure 1.

• Does the same conclusions hold true with an HSP70 inhibitor or siRNA?

• (OPTIONAL) There are a lot of discrepancies between Hsp90 inhibitors and effective treatment concentrations. For example, NVP-AUY922 caused purinosomes to disassemble whereas STA9090 cause purinosomes to change morphology and adopt a more aggregated state. Do other Hsp90 inhibitors share the same phenotypic response as NVP-AUY922 in this study.

• The treatment time (24 h) with NVP-AUY922 is very long. Given that Hsp90 interacts with hundreds of proteins, it is hard to understand whether the effect of Hsp90 inhibition is direct or indirect. Shorter times (1 h or less) would be more insightful.

__Response: __To address these specific comments on the specificity of effects from HSP90 inhibitor treatment, we have conducted additional experiments using NVP-AUY922, in addition to another HSP90 inhibitor, 17-AAG, and the HSP70 inhibitor, MKT-077, at both 24-hour and 1-hour timepoints.

Our results demonstrate that NVP-AUY922 can rescue the aggregated HPRT phenotype in WDR62 KO cells even after 1 hour of treatment (Fig. 6F, G). Similarly, 17-AAG exhibits a comparable effect, reinforcing the role of HSP90 inhibition in modulating the spatial distribution of HPRT in the cytosol (Fig. 6F, G). Additionally, we found that MKT-077, a HSP70 inhibitor, also rescues the aggregated HPRT phenotype, with the effect being most pronounced at 24 hours but still evident at 1 hour (Fig. S10A, B). We also utilized BAG2 siRNA but determined that BAG2 depletion rescued WDR62 KO effects on HPRT expression (Fig. 6L) but did not reverse the effect on HPRT spatial distribution (Fig. S10C).

(OPTIONAL) Does the 2.6-fold increase in BAG2 increase its association with WDR62?

Response: We observed a ~2.6-fold increase in BAG2 levels following WDR62 deletion (Fig. 6A). However, as WDR62 is not present in KO cells, it is not possible to verify whether there would be an increase association with WDR62 and we did not conduct an experiment to overexpress BAG2 in WT cells. However, we presume that increased cellular levels of BAG2 would lead to increased pulldown with WDR62 by immunoprecipitation for example.

Is the degradation of HPRT occurring through BAG2-mediated proteasomal degradation? Showing HPRT recovery by treating the cells with MG132 along with CHX would provide meaningful clues as to how BAG2 and HPRT might be related - Is BAG2 concentration increasing to facilitate the enhanced degradation of HPRT?

__Response: __We thank the reviewer for this useful suggestion. However, our initial experiments with MG132 and chloroquine to inhibit proteosomal and autophagic pathways respectively gave mixed results. Our preliminary findings suggest neither was sufficient to substantially rescue HPRT levels in WDR62 KO cells. However, this needs extensive follow up with more precise dissection of cell degradation pathways with additional inhibitor or genetic targeting of degradation machinery. Thus, we did not include these studies in the revision and will instead include this in a follow up paper once we have completed a more comprehensive investigation.

Does HPRT colocalize with WDR62 in cells?

__Response: __ In response to this comment, we have demonstrated that osmotic stress induces the spatial reorganisation of endogenous HPRT into puncta that juxtapose and co-localize with WDR62 granules in a stress-dependent manner (Fig. 6H). This was further validated by examining the endogenous WDR62-HPRT interaction using PLA, which also revealed a stress-induced increase upon sorbitol treatment (Fig. 6I).

(OPTIONAL) It would be nice to see validation experiments of some of the hits in Figure 1D or 1E in a co-immunoprecipitation experiment conducted similar to Figure 1C.

__Response: __Our BioID assay, presented in Fig. 1D and E, identified WDR62 interactors, such as AURKA, JNK, CEP170 and MAPKBP1, that have been previously validated by co-IP by our group and others. Among the chaperones identified, we focused on BAG2 in this particularly study and validated BAG2-WDR62 interactions between by coIP (Fig. 2) and by proximity ligation assays (Fig. 4).

The authors presented the findings that suggest that BAG2 interacts differently with commonly observed WDR62 mutations in MCPH2? How do these mutations affect WDR62 condensation, colocalization with purinosomes, or alter HPRT activity? Tying back the observations to something clinical would help elevate the overall significance of the findings.

Response: We investigated the condensation of mutant WDR62. Interestingly, R438H mutant, which binds BAG2 (Fig. 2), forms granules constitutively prior to stress treatment while the 3936dupC mutant, which does not bind BAG2 (Fig. 2), did not form granules in response to sorbitol stress treatment. We also find that PFAS is colocalized with R438H granules in the absence of stress, although this requires repeated analysis and quantification. However, WDR62 deletion does not prevent PFAS or PPAT granule formation (Fig. S6) and, given reviewer advice to focus the topic of our revised manuscript, we have not included the effects of WDR62 mutations on granule formation in our revised manuscript.

However, in response to these comments, we have conducted rescue experiments with patient-identified MCPH mutant variants of WDR62. Expression of the R438H or 3936dupC mutant in WDR62 KO cells did not rescue HPRT to the same extent as full-length WDR62 with wild-type sequence (Fig. 6B). Additionally, attempts to restore BAG2 levels in WDR62 KO cells by expressing mutant WDR62 showed no discernible difference from full-length WDR62. Thus, mutations to WDR62 associated with MCPH alters binding to BAG2 (Fig. 2, increased with R438H and decreased with 3936dupC), this was associated with dysregulated levels of BAG2 and HPRT. In our revised manuscript, we also examined the effect of HPRT depletion on neurodevelopment in vivo (Fig. 7) and included description of these findings at lines 417-442.

Are the text and figures clear and accurate?

1. There are many times throughout the manuscript that the wrong figure is being referenced. These mistakes caused significant confusion at many times while reviewing the manuscript. Please double check all in-text references to figures. For example, I believe that you meant to use Figure S1C instead of Figure 2E with the statement on lines 183-185. Again, I believe that correct figure reference on line 501 is Figure 7G not Figure 7E.

Response: We apologize for this oversight. We have amended the errors indicated by the reviewer. Line 544 (501 in first submission) now refers to the correct figure (Fig. 6F) and lines 204-206 (183-185 in first submission) correctly refers to Fig. S1C in addition to Fig 2E. Each of the authors have also revised the rest of the manuscript to ensure all figures are correctly referenced in the main text.

The figure legend on Figure S4 does not match the figure and the main text references. Please verify that the text in the figure legends correspond correctly to the figure.

Response: We apologize for these inconsistencies in the figure legend relating to Fig S4 in our original submission. In the revised manuscript, we have amended the figure legend and the main text referencing Fig. S4 to correctly correspond to order of data panels in this figure.

Please provide this data for the sentence on lines 399-400 in the supplemental file.

__Response: __As requested, we have revised the manuscript to include results on HPRT cytoplasmic localisation following osmotic stress. We show that osmotic stress induces the spatial reorganisation of HPRT into puncta that juxtapose and co-localize with WDR62 granules in a stress-dependent manner (Fig. 6H). This was further validated by examining the endogenous WDR62-HPRT interaction using PLA, which also revealed a stress-induced increase upon sorbitol treatment (Fig. 6I).

I believe that the authors use the phrase "cell proliferation" to describe cell viability in the main text. In the Materials and Methods section, the authors state "The XTT cell proliferation assay enables quantification of cellular redox potential, providing a colorimetric readout of cell viability." Cell proliferation, viability, and cytotoxicity are different measurements, so please revise to reflect the correct experiment that was performed.

__Response: __The XTT colorimetric assay can be used to determine cell proliferation or loss of cell viability depending on the specific experiment. The reviewer is correct in pointing out that our study using XTT to measure cell numbers in the context of purine-depletion (Figure 5B) is a measure of cell viability. We apologize for the misleading text in our description of the XTT methods in our original submission. In our revised manuscript, we have amended our description of the XTT assay in our methods and in the figure legend to more accurately reflect the experiment performed.

Other Minor Comments:

1. Move the sentence "In contrast, despite reduced mRNA..." (lines 387-388) to the last section when a reduction in PFAS expression was first mentioned.

__Response: __As requested, we have moved this line referring to PFAS protein levels in WDR62 KO cells to the previous section to when a reduction in PFAS mRNA was first mentioned.

1. Please reference the following in the manuscript: • BioGRID database in the main text and Materials and Methods section • The reported study showing the DNAJC7-WDR62 interaction (as curated from BioGRID) • Fiji in the Materials and Methods section

__Response: __We have now included references to these in our revised manuscript. References to BioGRID database are in the main text (line 146) and in the Materials and Methods (line 765). The report of DNAJC7-WDR62 interaction (Ref #37) curated from BioGRID was added at line 157 and reference (Ref #82) to Fiji plug-in was indicated at line 690 in Materials & Methods.

(Line 461-463) The authors state the following: "the loss of WDR62 leads to an increase in BAG2 and vice-versa (Fig. 7A) (Fig. S9B). I am not sure that the vice-versa (i.e. loss of BAG2 increases WDR62) is true. From the data presented in Figure 7H, I do not see a significant change in WDR62 expression upon BAG2 siRNA treatment.

__Response: __We apologize for the incorrect use of the term “vice versa” in this context. We had meant that while WDR62 loss led to an increase in BAG2, the converse increased expression in WDR62 resulted in a decrease in BAG2 levels. The reviewer is correct that the siRNA knockdown in BAG2 did not substantially alter WDR62 levels. We have amended the text at lines 465-467 to clarify this statement.

For your BioID study, do you know how many or the proportion of cells that were mitotically arrested with the low dose of nocodazole (200 ng/mL)? Given the small number of unique proteins that were in the mitotic only population, it is curious to know how enriched the cells were and whether WDR62 localization is important in the context of this study.

__Response: __The overnight treatment with low dose nocodazole results in an enrichment of cells arrested in late prometaphase which we estimate at 50-60% of AD293 cells compared to

1. Just to clarify, the WDR62-HA lane (third in each set) in Figure 1C is not WDR62-BirA*-HA and that it is only being used as a control.

Response: This is correct. To improve clarity, we have amended the labels on the WDR62-HA lanes in Figure 1C to say “WDR62-HA only”.

1. In the Discussion (lines 439-441) "We also show that WDR62 forms dynamic, phase-separated granules that co-localise with chaperones and purine metabolic enzymes, resembling purinosomes." I believe that the authors meant to say co-chaperones instead of chaperones given no microscopy data was presented showing the colocalization of HSP70/90 with WDR62 granules. Please revise.

__Response: __This sentence (line 473) has been revised as suggested.

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

Summary:

The authors provide evidence to reveal the novel functions of WDR62 protein in maintaining the stability and activity of purine metabolic enzymes and overall purine homeostasis. WDR62 interacted with BAG2, and they are recruited to purinosome. WDR62 loss caused accelerated degradation of purine salvage enzyme HPRT, and led to the accumulation of purine nucleotide intermediates.

While this study is compelling and significant for the field of neurodevelopmental disorders including microcephaly and purine metabolism, there are several concerns that should be addressed before publication.

__Response: __We thank reviewer #2 for their constructive criticisms and supportive comments noting the statement reinforcing significance of our study in the field. We have made a meaningful and concerted effort to address the reviewer comments with extensive additional experimental work and substantial revision of our manuscript.

Major comments:

Although all experiments are conducted using non-neuronal cultured cells, does this phenomenon also occur in neuronal cells?

__Response: __To address this comment and reviewer concerns regarding the links between WDR62 and HPRT in a neuronal context, we performed in utero-electroporation to determine the effects of HPRT depletion on formation of neocortex in mouse embryos. We electroporated embryonic day 14 (E14) mouse brains with siRNA targeting Wdr62, and Hprt and assessed neural progenitor proliferation, migration and differentiation using immunofluorescence. We find that the loss of both WDR62 and HPRT leads to a similar precocious delamination of neural progenitors from the apical ventricular surface (Fig. 7). This process is the first step in neural migration and required to generate a diversity of cells, both self-renewed (eg. outer radial glia) and differentiated neurons and glial cells in the developing neocortex (doi.org/10.1146/annurev-cellbio-101011-155801). Interestingly, we also uncovered that HPRT loss promoted the self-renewal of delaminated intermediate progenitors (IPs) which is unlike impaired the self-renewal of neural progrenitors observed following WDR62 depletion (Fig. 7). Thus, brain development is sensitive to HPRT levels and the HPRT depletion phenocopies WDR62 in cell delamination which supports a neural role for WDR62-HPRT. Moreover, our findings suggest WDR62 loss has more severe neurodevelopmental defects with hints at the complex metabolic functions of WDR62 (discussed in lines 563-577).

What is the interaction between endogenous WDR62 and Bag2? This is because in overexpression systems, multiple chaperones may interact with the target protein during protein folding.

Is endogenous WDR62 also present in the purinosome in purine depleted or sorbitol condition?

__Response: __In response to these comments and similar concerns by reviewer #1, we examined interactions between WDR62, BAG2, HPRT, and PFAS at the endogenous level by utilising proximity ligation assays (PLA, Fig. 4+6). We determined a robust interaction between endogenous WDR62 and BAG2 (Fig. 4K), evident by abundant PLA puncta which were nuclear excluded and localised to the cytosol, consistent with our results in overexpression systems (Fig. 4). We also confirmed endogenous WDR62 interactions with purine enzymes PFAS (Fig. 4K) and HPRT (Fig. 6I) in a similar fashion. To determine whether sorbitol stress promotes their interaction, we assessed changes in the per cell numbers of these puncta in response to sorbitol stress. We confirmed that endogenous WDR62 interaction with HPRT was dependent on BAG2 (Fig. 6J). WDR62-HPRT interactions increased with sorbitol stress (Fig. 6I).

Regarding Fig6 and Fig7, when HPRT decreases and inosine accumulates in WDR62-KO condition, did the levels of hypoxanthine, xanthine, and uric acid change?

__Response: __ In Fig. 5G we used an untargeted metabolomics approach that relies on identification databases such as MS-DIAL and associated spectral libraries. Unlike targeted approaches, this method does not always allow for the confident identification of all metabolites of interest. As a result, hypoxanthine, xanthine, uric acid, and other purine intermediates (e.g., AICAR) were not positively identified. This is likely due to limitations in database coverage, spectral similarity to other compounds, or constrains related to our extraction method.

Does HPRT and the three microcephaly-associated WDR62 mutants also recruited in the purinosome in purine depleted or sorbitol condition?

__Response: __In response to this, and a similar comment by reviewer #1, we examined whether endogenous HPRT co-localised with WDR62 granules induced by sorbitol. We show that hyperosmotic stress induces the spatial reorganisation of HPRT into puncta that juxtapose and co-localize with WDR62 granules in a stress-dependent manner (Fig. 6H). This was further validated by examining the endogenous WDR62-HPRT interaction using PLA, which also revealed a stress-induced increase upon sorbitol treatment (Fig. 6I).

As to whether mutant WDR62 was recruited to purinosomes, as detailed in our response to reviewer #1 above (minor comment #6), we find that R438H mutant formed condensed granules prior to stress treatment while 3936dupC mutant did not form granules in response to stress. Therefore, MCPH mutations appear to disrupt the stress-induced formation of WDR62 granules in the cytoplasm. Since we also find that WDR62 KO did not prevent stress-induced formation of PFAS and PPAT granules, which may represent or overlap with purinomes, we chose to not include our findings on granule localization of mutant WDR62 localization in our current revised manuscript. We instead focused on rescue of HPRT and BAG2 levels with patient-derived MCPH mutant variants of WDR62. We confirmed that, unlike WT WDR62, mutant WDR62 could not fully return HPRT or BAG2 levels in WDR62 KO cells (Fig. 6B).

In Fig7C, HPRT/tubulin ratio appears to decrease in WT from 0hr to 24h, but the graph does not show this decrease. Additionally, quantification of PFAS(FGAMS) and BAG2/tubulin should be performed.

Response: While slight variations in HPRT signals are visible from 0 h to 24 h in the representative blot, quantification across the n = 9 biological replicates do not support a significant decrease, with these variations falling within the SEM shown in the graph. This representative blot was selected for its clarity and since it most clearly depicts the key trend which is the increasing difference in the HPRT/Tubulin ratio between WT and KO cells with increased duration of CHX treatment. Additionally, in response to this comment, we have now quantified PFAS and BAG2/Tubulin and have inserted these data into Fig. 6C.

Fig7D is problematic. HPRT in WDR62-KO cells seems to localize in the nucleus, possibly due to stronger exposure in KO conditions compared to WT. Also, the line scan is drawn in areas with low signal in WT. The comparison should be performed in areas with high perinuclear signal.

__Response: __We appreciate the reviewer’s feedback and acknowledge their concern of an apparent differences in fluorescence intensity in WDR62 KO vs WT cells. In the original submission, slight differences in fluorescence intensity between the WT and WDR62 KO panels may have exaggerated differences in HPRT levels in the nucleus. To address this, we have replaced the representative images with those with more consistent fluorescence intensity across conditions and better represent the average population of sampled cells. Regardless, quantified the change in HPRT cytoplasmic redistribution in response to WDR62 loss across multiple independent biological replicates (n=4) and multiple cells (>12 cells per repeat) within each biological replicate to confirm a change in HPRT distribution in KO cells (Fig. 6E+G).

The localization of HPRT should be compared in WT and WDR62-KO with BAG2 siRNA. It is also possible to confirm whether the phenotypes observed in KO, such as cell proliferation and xanthosine/inosine levels, are rescued.

__Response: __We conducted a series of immunofluorescence experiments to assess the impact of BAG2 knockdown (siRNA) on the spatial distribution of HPRT in WT and WDR62 KO cells. BAG2 depletion had no effect on HPRT distribution and did not rescue its aggregated-like appearance in WDR62 KO cells (Fig. S10C). Thus, while abnormal HPRT localization in absence of WDR62 was due to excessive of HSP70/90 activity (Fig. 6F), this was not reversed by BAG2 siRNA. However, BAG2 siRNA reduced BAG2 levels to below wild-type cells (Fig. 6I). An imbalance of HSP and co-chaperone levels are known to be involved in aggregation of cytoplasmic proteins. (doi.org/10.1096/fj.202002645R). Therefore, while BAG2 siRNA may have returned HPRT levels, it may not have appropriately corrected the levels of HSP70/90 activity required for normal HPRT localization (lines 407-413 in revision).

We did not attempt to rescue cell proliferation and xanthosine/inosine levels with BAG2 siRNA in order to prioritize other studies requested by reviewers such as neurodevelopment function of HPRT and flux analysis of purine synthesis/salvage.

It should be considered that the induction of Bag2 in WDR62-KO might allow purinosome formation to proceed normally due to compensation. The co-localization of WDR62 and purine enzymes during purinosome formation should be compared when BAG2 expression is suppressed. Similarly, any changes in BAG2 localization in WDR62-KO should be examined. Furthermore, the purinosome formation ability should be compared in WDR62KO + Bagl2 siRNA condition.

__Response: __To address these insightful comments and requests by reviewer #2 response, we have performed additional experiments to assess whether BAG2 facilitates WDR62 granule assembly, purinosome assembly, and the WDR62-HPRT interaction. siRNA-mediated BAG2 depletion did not prevent stress-induced assembly of WDR62 or PFAS granules (Fig. S6D+E). Thus, unlike HSP70/90 activity, purinosome assembly and WDR62 localization to purinosomes did not appear to require BAG2. Rather we demonstrated a role for WDR62-BAG2 in regulating HPRT (Fig. 6, lines 400-411).

The reduction of HPRT in WDR62-KO should be examined for potential effects of enhanced degradation via the ubiquitin-proteasome system or the autophagy-lysosome system.

__Response: __See our response to reviewer #1, minor comment #3. Briefly, neither MG132 blockade of proteosomal degradation nor chloroquine inhibition of autophagy was sufficient to return HPRT levels in WDR62 KO cells. However, these studies are not exhaustive and we are currently pursuing alternative and more specific inhibitors of UPS or lysosomal degradation. As this is not essential for the main findings of the current manuscript, we will include delineation of HPRT degradation pathway in a future publication.

Although it is known that HPRT-KO mice do not exhibit any effects on normal brain development except in some dopaminergic neurons, what are your thoughts on this?

Response: We thank the author for raising this interesting point. While global HPRT KO mice appear not to exhibit widespread brain development defects (doi: 10.1007/s00018-022-04326-x) this does not preclude a role for impaired HPRT to contribute to specific neurodevelopmental defects in context of WDR62 mutation or loss. In utero electroporation studies, we find that WDR62 or HPRT depletion results in precocious delamination of apical precursors which may trigger premature differentiation. However, while WDR62 depletion led to reduced proliferation of delaminated radial glia ventricular/subventricular zone, we observed increased proliferation with HPRT loss (Fig. 7). Our findings are in good concordance with the study mentioned by reviewer #2, Witteveen et al. 2022 (doi: 10.1007/s00018-022-04326-x), who similarly reported an increase in proliferation and abnormal cell migration patterns which may be attributed to apical delamination of radial glia. The increased proliferation of progenitors in the intermediate zone or outer ventricular/subventricular zone may compensate for premature differentiation of apical progenitors to explain the lack of overall reduction in brain size with HPRT deficiency alone. Thus, our findings indicate that defects in WDR62-HPRT may contribute to the premature apical delamination of radial glia but WDR62 has additional functions that are indispensable for normal brain development. This may include complex functions in regulating purine metabolism independent of HPRT. We have now included the paper by Witteveen et al. 2022 in our revised manuscript and the above was discussed in detail at lines 565-577.

Minor comments: • Please write the full name before the abbreviation of the gene. • There is no measurement data for Fig7C, and a measurement line is drawn only in one panel of the ROI. • The line 488 "Fig11" looks like a typo.

__Response: __As requested by the reviewer, we have included the full name of genes before their abbreviation and corrected the typographical error (line 548 in revision). For Fig S7C (Fig. S6B in revision), we have removed the measurement line which was included in error in our original manuscript. This supplementary figure demonstrates that the stress-stimulated granule assembly of ectopically expressed PFAS and PPAT was not altered or appreciably different in WDR62 KO cells. We quantified this for sorbitol treatment (Fig S6A). We performed the purine-depletion experiment twice with identical results. Given this was a negative result we focused our efforts elsewhere.

The table could not be found.

__Response: __We apologise for this oversight. The Supplementary Information file containing Tables S1-3 was excluded from the original submission has now been included in our revised submission.

It is strange that all measurement values for WT or control in Fig2, Fig7, and FigS9 are exactly 1.0 without any variation. Please check the measurement method again.

__Response: __Our densometric band measurements in western blots within the indicated figures are normalized against WT control cells as a reference condition. This removes variation in arbitrary densitometric values that changes from blot to blot even for identical samples. Thus, values are fold-change in protein levels relative to WT control conditions. Hence values for WT or control cells are 1 (no change relative to itself) as the reference points and there is no variation between replicate experiments. We apologize for not explaining this in our original submission. Our revision now describes this quantification and processing of raw data in methods and materials (lines 668-671).

Please write the method for purine depleted medium.

__Response: __Our revised manuscript includes description of how we depleted cells of purines in the Materials & Methods at lines 636-640 with reference to source materials and prior studies.

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

Summary:

In the present work, authors describe a novel role of the microcephaly associated protein WDR62 in purine metabolism under cell stress conditions. In the proposed cellular model (AD293 WDR62 overexpression system), the WDR62 proximity binding partners are firstly identified and categorized according to their functional role in the cell (protein folding, purine metabolism, and stress granules). Among them, authors focus on BAG2 - a HSP70/90 co-chaperone involved in cellular stress responses. After the characterization of the WDR62-BAG2 physical interaction sites, suggested to be disrupted by WDR62 pathogenic mutations, their functional interaction in cellular stress responses is investigated. WDR62-associated granules are extensively characterized for their physical and dynamic properties under different conditions (i.e., hyper-osmotic stress). Further, through the evaluation of N-and C-terminally truncated form of WDR62 authors characterize the protein regions responsible for WDR62-containing granule condensation - suggesting a potential mechanism disruption in the event of pathological WDR62 mutations. Lastly, authors provide evidence that WDR62 condensation does not occur in canonical stress granules but in the so called-purinosomes, where it participates in the regulation of purine metabolic pathway stabilizing HPRT (purine salvage enzyme) via WDR62-BAG2-HSP70/90 axis.

Major comments:

Overexpression system and the employed cell line are a major limitation of the study. There is no experimental data on human neural cells and on endogenous WDR62, underestimating the potential difference in cell type-specific metabolism. In light of this consideration, the provided introduction and conclusions on neural development and microcephaly have to be re-formulated. I suggest providing a more general introduction/conclusions on WDR62 role (and alterations) in cell division and cell metabolism (neurodevelopment and cancer share common patterns) since purine homeostasis is not exclusive of neural progenitor cells.

This reviewer thinks that the structure of the work is a bit convoluted (too many results in main figures that are not substantial). I suggest to re-organize and to prioritize the most relevant results. Further, it would be clinically relevant to add WDR62 mutant constructs in the functional evaluation of purine metabolism to better dissect the physiological role of WDR62 and the impact of the mutations on cellular physiology.

Response: We are appreciative for this constructive evaluation of our manuscript and frank comments on the limitations of our study from reviewer #3. We have now included extensive new studies that provide evidence supporting endogenous mechanisms and insights into in vivo functions in neurodevelopment. We have also removed and combined several figures relating to the stress-induced purinosome assembly of WDR62 to better focus our manuscript on WDR62 interaction mechanisms and their purine metabolic function.

Fig. 1: Overexpressed WDR62 fluorescence signal might be artifactual and may hide more detailed localization pattern during interphase. Authors should also provide endogenous WDR62 immunofluorescence panel in AD293 cells. Additionally, the "cytosolic" localization of WDR62 during interphase (indicated in the introduction, lines 88-89) has been re-defined in recent works pointing out that the protein is dynamically associated with the interphasic centrosome, the Golgi apparatus, and spindle poles during mitosis.

__Response: __In response to this point, we have added text in the introduction (line 100-102) to clarify the dynamic association of WDR62 in cytoplasmic compartment during interphase includes the golgi apparatus. We have also added reference to the study by Dell’Amico and co-workers (doi: 10.7554/eLife.81716, Ref #24 in revision) alluded to by reviewer #3.

We utilized ectopic expression of tagged WDR62 constructs to determine redistribution to stress-responsive cytoplasmic granules and co-localization with purine enzymes. Immunofluorescence staining of endogenous WDR62 also appears to reveal granule assembly but these findings are not as clear as the primary antibodies also detect additional proteins independent of WDR62 (validated using our KO cells). We agree that protein overexpression may result in artificial localization patterns but this can be mitigated with careful controls. We find that stress-induced WDR62 granule localization is highly dynamic and reversible. We observe the same response with full-length protein using different fluorescent protein or small affinity tags at either N- or C-terminus. High expression of mutant WDR62 (e.g. 3936dupC) or a closely related family member (MAPKBP1) do not form the same purinosome-associated granules. Moreover, in response to related comments by reviewer #1 and #2, we have now included proximity ligation assays confirm interactions between WDR62, BAG2 and purine enzymes (Fig. 3 and Fig. 6).

Fig. 1C lacks quantification of BAG2/CEP170/AURKA signal. Further, how can authors exclude that is not nocodazole effect on microtubules disruption which impairs WDR62 spindle pole localization and therefore protein-protein interactions? A panel showing that "low dose" nocodazole do not impinge endogenous and exogenous WDR62 localization in mitotic cells is needed.

__Response: __WDR62-BirA specific biotinyation and affinity isolation of BAG2, CEP170 and AURKA, compared to BirA or WDR62-HA only controls, was very clear in Fig. 1C. We did not quantify the extent that mitotic synchronization increased or decreased binding to WDR62 as the mitosis specific context was not a focus in our subsequent figures. Rather we focused on and quantified in detail WDR62-BAG2-HPRT mechanisms in response to cell stress.

We are also very confident that low dose nocodazole treatment does not prevent spindle pole localization. This treatment impinges on microtubule dynamics to trigger spindle checkpoints, arresting cells in mitosis. The bipolar organization of spindles is lost but spindle microtubules and minus-end microtubule directed localization of WDR62 at spindle asters are retained under these conditions and is specific to mitotic cells. The robust WDR62-BirA biotinylation of AURKA, which is spindle pole-associated, specifically in mitotic arrested cells further confirms WDR62 is retained at the spindle. We demonstrated this in our previous papers (Ref. 5+6). Others have also shown that both endogenous (doi: 10.7554/elife.81716) and exogenous WDR62 (doi: 10.1083/jcb.202007167, doi: 10.1242/jcs.157537) retain spindle pole localisation under similar conditions.

Fig. 3 H-J: The fluorescence signals are saturated (also evident in the intensity profile plot) and thus not applicable for any analysis. Further, how these linear ROIs are chosen? The signal pattern is not homogenously distributed in those images. Please provide a more consistent fluorescence analysis.

__Response: __We acknowledge reviewer #3 concerns but while some granules, particularly those expressing G3BP-EGFP, exhibit saturated fluorescence signals, this does not impact or prevent our analysis. Our aim was not to quantify subtle fluorescence intensity changes within individual granules, but rather to compare fluorescence signal between granules across different channels to identify overlap. The linear ROIs were selected at random to illustrate that WDR62 and G3BP signals do not overlap between WDR62 and G3BP-positive granules.

Minor comments:

Abstract, line 49: How can these WDR62 mutations can result in a complete loss of the protein ("In cells lacking WDR62") if authors report co-IP experiments (Fig. 2) with clear mutant WDR62 bands? Rephrase accordingly.

__Response: __The statement in our original abstract referenced by reviewer #3 referred to results presented in Fig 7 (now Fig. 6 in our revision) comparing WDR62 KO with WT cells and not co-IP experiments with mutant WDR62 in Fig 2. We have revised our abstract substantially to incorporate additional experimental work and to ensure clarity in our statements related to KO cells lacking WDR62 and cells expressing WDR62 mutants.

Result referred to Fig. 2D reports that "BAG2 co-immunoprecipitated with WDR62(N)-EGFP but not WDR62(C)-EGFP". The blot and the relative quantification in figure 2D instead show BAG2 signal in the WDR62(C)-EGFP - even if significantly lower. Please rephrase accordingly.

__Response: __We have revised line 192 of the main text to more accurately state the reduced interaction between WDR62(C)-EGFP and BAG2.

Lines 186-187: authors declare that the C-terminal tail comprising the helix-loop-helix domain is required for BAG2 to bind full-length WDR62. There are no such data in support of this. The C-terminal fragment includes both the disordered region and the dimerization domain. How can authors conclude that the dimerization domain alone is sufficient to bind BAG2?

__Response: __In Fig. 2, we show that the co-IP of BAG2 was significantly impaired in cells expressing WDR62(3936dupC), which lacks the C-terminal helix-loop-helix (HLH) domain. Additionally, we demonstrate that the C-terminal half of WDR62, which includes the HLH domain, does not bind BAG2. Based on these findings, we conclude that while the HLH domain is necessary for BAG2 binding to full-length WDR62, it is alone not sufficient. To ensure clarity, we have revised the main text (lines 207-209) to state “…the C-terminal helix-loop-helix domain—required for WDR62 dimerisation—is necessary but not sufficient for BAG2 to bind full-length WDR62.”

Lines 189-190: results in AD293 cell line are not directly applicable in demonstrating that poor WDR62-BAG2 interaction can lead to alterations in brain development. Please rephrase.

__Response: __We established that WDR62 interacts with BAG2 co-chaperone and MCPH mutations in WDR62 disrupt this interaction. Although our results were performed in AD293 cells, it seemed reasonable to speculate that WDR62 interactions with chaperones might contribute to brain development given well established WDR62 functions in this context. However, we acknowledge that this speculation may not be appropriate at this point of the manuscript, so we have removed this text (line 210) in our revised manuscript.

Line 196: Indicate here, as the first mention, stress granules as "SGs" and use the abbreviation consistently throughout the manuscript.

__Response: __We have abbreviated stress granules as suggested (first mentioned at line 102) and utilized this abbreviation consistently throughout the manuscript.

Line 255: are human neural progenitor cells enough sensitive to sorbitol? If not, the proposed experimental design is a bit artifactual and the results/conclusions cannot be related to neural development alterations. I suggest applying more "physiological" stressors and frame the results in meaningful neurodevelopmental/tumorigenic environment. Please add this point to the discussion.

__Response: __Neural progenitors are likely sensitive to sorbitol, as hyperosmotic stress has been used to induce phase separation of a wide variety of proteins in neural contexts (doi: doi.org/10.1038/s41598-023-39090-w, doi.org/10.1016/j.celrep.2018.06.094). In this study, we leveraged sorbitol-induced hyperosmotic stress as a controlled and reproducible means of triggering WDR62 phase separation, enabling us to examine its downstream interactions with BAG2, HPRT, and other purine enzymes. We further extend these observations to metabolic cell stress with purine-depletion.

We found that WDR62 phase separation occurs rapidly at low sorbitol concentrations (~50 mM) (Fig. 3B), suggesting that even milder osmotic stress, particularly under prolonged exposure, could similarly drive WDR62 condensation in physiological settings. As requested by the reviewer, we have added a small section to the discussion (lines 472-480) to discuss the physiological implications of sorbitol stress on WDR62 granule assembly.

Line 240: WDR62 granules association with microtubules and especially mitochondria is not convincing (Fig. S5). This data seems to be a bit qualitative, please provide more detailed quantification of this parameter.

__Response: __The association of WDR62 granules with microtubules and mitochondria is quantitatively assessed using two methods, as shown in the graphs to the right of the images. One graph presents the proportion of WDR62 granules overlapping with CytC/Tubulin, providing a binary measure of colocalization. We also examined the degree of signal correlation across the entire ROI by calculating Pearson’s correlation coefficient. In response to sorbitol, we showed a higher association of WDR62 with Tubulin and CytC compared to randomised controls. We have updated the Materials and Methods to include a detailed description of this analysis (lines 708-720).

Fig. 4 is convoluted. I suggest moving some data to supplementary to improve the clarity of the figure.

__Response: __In addressing this comment and related comments from other reviewers to focus our manuscript, we have removed our data on fluorescence recovery and post-stress disassembly of WDR62 granules from what was Fig. 4 in our original submission and combined remaining components with Fig. 3 to centre on stress-induced assembly of WDR62 granules for our revised manuscript.

Line 273: "Liquid-like protein condensates also exchange their contents with the bulk cytosol [52]". Reference 52 reviews the existing literature referred to biomolecular condensates that exert nuclear function (e.g., genome organization, gene expression, and DNA repair). No mention on events involving cytoplasm. Please add a more relevant reference.

__Response: __We thank the reviewer for highlighting this inconsistency. However, this reference is no longer required and has been removed from our revised manuscript as the section of the main text has been deleted in alignment with the above response where figure panels relating to WDR62 phase separation were removed for focus and clarity.

Lines 290-291: have authors considered the effect of sorbitol on microtubules dynamic that might reflect in granules dynamic changes?

__Response: __We thank the authors for this insightful comment. Hyperosmotic stressors such as sorbitol are known to reduce microtubule dynamicity (doi.org/10.1016/j.devcel.2022.02.001), likely due to increased cytoplasmic viscosity and crowding effects. While we have not directly assessed microtubule dynamics in our study, it is certainly possible that these changes could influence WDR62 granule dynamics, given their association with microtubules (Fig. S6). While we have reduced emphasis on the dynamic nature of WDR62 granules in our revision, a useful direction for future studies to explore how alterations in microtubule dynamics induced by physiological stressors facilitate changes in WDR62 granule assembly or dynamics (e.g., fission, fusion).

Line 295: I suggest moving the prediction of the disordered region of WDR62 when first mentioned (e.g., Supplement referred to Fig. 2)

__Response: __This text is no longer required as we have removed this dataset from our revised manuscript to address reviewer consensus feedback to enhance cohesiveness and clarity.

Fig. S6C-E, I: Unclear which is the criterion by which a cell is marked as "with" or "without" granules.

__Response: __This text is no longer required as we have removed this dataset from our revised manuscript to address reviewer consensus feedback to enhance cohesiveness and clarity.

Fig. S8: Unclear, also from the micrograph showed in the figure, how authors have counted/considered the microtubules/mitochondria associated purinosomes. Seems very qualitative and observer dependent. Please provide a more reliable analysis.

__Response: __We apologise for omitting a description of the methodology used in the analysis of the images in Fig. S8 (now Fig. S6 in revision). We have now provided a detailed description in the Materials and Methods section (lines 709-721) of how microtubule- and mitochondria-associated purinosomes were identified and quantified.

Fig. 6A: The same blot of WDR62 KO is shown in Fig. S7. Please remove one.

__Response: __As requested, we have removed a set of blots demonstrating WDR62 protein deletion in KO cells from Fig. S7 (Fig. S6 in revision).

Fig. 6C, D: Method for cell proliferation measure is indirect and "rounded cells" as indicator of cell death is sub-optimal. Analysis with specific markers would be preferable in both cases.

Response: We used an XTT assay to measure cell viability as a function of cell number. In revised text, and also detailed in our response to reviewer #1 (point 4 under Text and Figures), we clarified that this was a measure of cell viability in response to purine-depletion as oppose to a direct measure of cell proliferation. Our amended text attributes the results in Fig 6C (now Fig. 5B in revision) to changes in cell viability rather than proliferation.

With regards to additional measure of cell death, we had also performed LDH release assays to quantify cell death in addition to our measurement of cell rounding. The LDH assay is widely used and accepted measure of cell death or cytotoxicity and is indicated in Figure 5D in the revision.

Fig.7B: Why the transfection control vector "EGFP only" significantly increases/decreases the BAG2/HPRT expression with respect to the negative control?

__Response: __The reviewer comment here on Fig. 7B (now Fig. 6B in revision) refers to the control vector (EGFP only) transfected into WDR62 KO cells, as opposed to WT cells. Therefore, the difference in protein expression in this condition does not match the WT cells in the first lane as BAG2 and HPRT are increased and decreased respectively in KO cells compared to WT. This aligns with results presented in Fig. 6A.

Paragraph from line 410 to 434: very confusing, the reported results are not well conveyed and therefore not convincing. To be reformulated.

__Response: __We thank the reviewer for the direct and constructive feedback. The revised section (lines 378–416) addresses whether WDR62-BAG2 regulates HPRT levels. It has been substantially updated to include new experimental data and to reflect our latest findings and conclusions. We believe these revisions have significantly improved the logical flow and clarity of the discussion.

Lines 524-526: the author's conclusion that: "...the loss of purine metabolic enzymes, including HPRT, disrupts neurogenesis, resulting in microcephaly, cell cycle defects, ciliopathies, and abnormalities in proliferation and neural progenitor fate decisions, mirroring the loss of WDR62." is not supported by the cited literature [29] and by the results presented in this work. Please provide additional references or remove the statement.

__Response: __ As requested by the reviewer, we have removed the statement and substantially revised this section of the discussion (lines 563-677) to incorporate findings from our additional studies such as in utero electroporation.

Lines 527-529: if authors state that "...other WD repeat-containing and microcephaly-associated proteins interact with purine enzymes..." have to provide additional references in addition to the NWD1 one. Otherwise, these lines should be rephrased as "another WD repeat containing and microcephaly-associated protein...".

__Response: __We have amended this statement (line 589-592 in revision) as requested.

Reference 62 is not well indexed in the Reference section. Please adjust.

__Response: __We thank the reviewer for pointing out this error. The reference to Rauch et al. (2014) [Ref. 60 in the revised manuscript] has been corrected and now includes the complete bibliographic details.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In the present work, authors describe a novel role of the microcephaly associated protein WDR62 in purine metabolism under cell stress conditions. In the proposed cellular model (AD293 WDR62 overexpression system), the WDR62 proximity binding partners are firstly identified and categorized according to their functional role in the cell (protein folding, purine metabolism, and stress granules). Among them, authors focus on BAG2 - a HSP70/90 co-chaperone involved in cellular stress responses. After the characterization of the WDR62-BAG2 physical interaction sites, suggested to be disrupted by WDR62 pathogenic mutations, their functional interaction in cellular stress responses is investigated. WDR62-associated granules are extensively characterized for their physical and dynamic properties under different conditions (i.e., hyper-osmotic stress). Further, through the evaluation of N-and C-terminally truncated form of WDR62 authors characterize the protein regions responsible for WDR62-containing granule condensation - suggesting a potential mechanism disruption in the event of pathological WDR62 mutations. Lastly, authors provide evidence that WDR62 condensation does not occur in canonical stress granules but in the so called-purinosomes, where it participates in the regulation of purine metabolic pathway stabilizing HPRT (purine salvage enzyme) via WDR62-BAG2-HSP70/90 axis.

Major comments:

Overexpression system and the employed cell line are a major limitation of the study. There is no experimental data on human neural cells and on endogenous WDR62, underestimating the potential difference in cell type-specific metabolism. In light of this consideration, the provided introduction and conclusions on neural development and microcephaly have to be re-formulated. I suggest providing a more general introduction/conclusions on WDR62 role (and alterations) in cell division and cell metabolism (neurodevelopment and cancer share common patterns) since purine homeostasis is not exclusive of neural progenitor cells.

This reviewer thinks that the structure of the work is a bit convoluted (too many results in main figures that are not substantial). I suggest to re-organize and to prioritize the most relevant results. Further, it would be clinically relevant to add WDR62 mutant constructs in the functional evaluation of purine metabolism to better dissect the physiological role of WDR62 and the impact of the mutations on cellular physiology.

Fig. 1: Overexpressed WDR62 fluorescence signal might be artifactual and may hide more detailed localization pattern during interphase. Authors should also provide endogenous WDR62 immunofluorescence panel in AD293 cells. Additionally, the "cytosolic" localization of WDR62 during interphase (indicated in the introduction, lines 88-89) has been re-defined in recent works pointing out that the protein is dynamically associated with the interphasic centrosome, the Golgi apparatus, and spindle poles during mitosis.

Fig. 1C lacks quantification of BAG2/CEP170/AURKA signal. Further, how can authors exclude that is not nocodazole effect on microtubules disruption which impairs WDR62 spindle pole localization and therefore protein-protein interactions? A panel showing that "low dose" nocodazole do not impinge endogenous and exogenous WDR62 localization in mitotic cells is needed.

Fig. 3 H-J: The fluorescence signals are saturated (also evident in the intensity profile plot) and thus not applicable for any analysis. Further, how these linear ROIs are chosen? The signal pattern is not homogenously distributed in those images. Please provide a more consistent fluorescence analysis.

Minor comments:

Abstract, line 49: How can these WDR62 mutations can result in a complete loss of the protein ("In cells lacking WDR62") if authors report co-IP experiments (Fig. 2) with clear mutant WDR62 bands? Rephrase accordingly.

Result referred to Fig. 2D reports that "BAG2 co-immunoprecipitated with WDR62(N)-EGFP but not WDR62(C)-EGFP". The blot and the relative quantification in figure 2D instead show BAG2 signal in the WDR62(C)-EGFP - even if significantly lower. Please rephrase accordingly.

Lines 186-187: authors declare that the C-terminal tail comprising the helix-loop-helix domain is required for BAG2 to bind full-length WDR62. There are no such data in support of this. The C-terminal fragment includes both the disordered region and the dimerization domain. How can authors conclude that the dimerization domain alone is sufficient to bind BAG2?

Lines 189-190: results in AD293 cell line are not directly applicable in demonstrating that poor WDR62-BAG2 interaction can lead to alterations in brain development. Please rephrase.

Line 196: Indicate here, as the first mention, stress granules as "SGs" and use the abbreviation consistently throughout the manuscript.

Line 255: are human neural progenitor cells enough sensitive to sorbitol? If not, the proposed experimental design is a bit artifactual and the results/conclusions cannot be related to neural development alterations. I suggest applying more "physiological" stressors and frame the results in meaningful neurodevelopmental/tumorigenic environment. Please add this point to the discussion.

Line 240: WDR62 granules association with microtubules and especially mitochondria is not convincing (Fig. S5). This data seems to be a bit qualitative, please provide more detailed quantification of this parameter.

Fig. 4 is convoluted. I suggest moving some data to supplementary to improve the clarity of the figure.

Line 273: "Liquid-like protein condensates also exchange their contents with the bulk cytosol [52]". Reference 52 reviews the existing literature referred to biomolecular condensates that exert nuclear function (e.g., genome organization, gene expression, and DNA repair). No mention on events involving cytoplasm. Please add a more relevant reference.

Lines 290-291: have authors considered the effect of sorbitol on microtubules dynamic that might reflect in granules dynamic changes?

Line 295: I suggest moving the prediction of the disordered region of WDR62 when first mentioned (e.g., Supplement referred to Fig. 2)

Fig. S6C-E, I: Unclear which is the criterion by which a cell is marked as "with" or "without" granules.

Fig. S8: Unclear, also from the micrograph showed in the figure, how authors have counted/considered the microtubules/mitochondria associated purinosomes. Seems very qualitative and observer dependent. Please provide a more reliable analysis.

Fig. 6A: The same blot of WDR62 KO is shown in Fig. S7. Please remove one.

Fig. 6C, D: Method for cell proliferation measure is indirect and "rounded cells" as indicator of cell death is sub-optimal. Analysis with specific markers would be preferable in both cases.

Fig.7B: Why the transfection control vector "EGFP only" significantly increases/decreases the BAG2/HPRT expression with respect to the negative control?

Paragraph from line 410 to 434: very confusing, the reported results are not well conveyed and therefore not convincing. To be reformulated.

Lines 524-526: the author's conclusion that: "...the loss of purine metabolic enzymes, including HPRT, disrupts neurogenesis, resulting in microcephaly, cell cycle defects, ciliopathies, and abnormalities in proliferation and neural progenitor fate decisions, mirroring the loss of WDR62." is not supported by the cited literature [29] and by the results presented in this work. Please provide additional references or remove the statement.

Lines 527-529: if authors state that "...other WD repeat-containing and microcephaly-associated proteins interact with purine enzymes..." have to provide additional references in addition to the NWD1 one. Otherwise, these lines should be rephrased as "another WD repeat containing and microcephaly-associated protein...".

Reference 62 is not well indexed in the Reference section. Please adjust.

Referees cross-commenting

This reviewer thinks that the points raised by reviewer #1 and #2 are very accurate and significant. Some of them are also shared between our three review reports and in general are referred to: clarity of the manuscript improvement, little consistency between the results displayed in the figures and the text/conclusions in some points, concerns about the reliability of some measurements/result and the employed cellular model, and the lack of endogenous protein data.

Significance

General assessment:

The here described new role of WDR62 in purine metabolism and the proposed pathway are novel and relevant to shed light on pathophysiological cellular and molecular mechanisms that potentially underlie neurodevelopmental defects and carcinogenesis - processes in which WDR62 is implicated. The experimental design is extended and generally well-conceived even though quite dispersive in some points.

The strength of the work resides in its versatility - making these findings potentially applicable to different cell types and different contexts (e.g., from neural development to malignancies) - and in the protein-protein interactions characterization under several conditions.

Similarly, the major weakness is the generalist trait of the findings that describes WDR62 cellular behavior mostly in an over-expression system in an immortalized cell line, underestimating the intrinsic metabolic and protein expression-level differences among cell types.

Advance:

WDR62 is a scaffold protein with pleiotropic functions and a plethora of molecular interactors. Literature reports many molecular pathways involving WDR62 mainly in cell cycle progression, primary cilia biogenesis and centrosomal functions in a neurodevelopmental context. In the present work, authors describe mechanistic insights of a never reported WDR62-BAG2-HSP70/90 molecular pathway shedding new light on the role of this protein in cellular metabolism thus providing a new perspective on WDR62 pathophysiological functions.

Audience:

Basic research audience will be interested in this research work. The described molecular pathway involving WDR62 in purine metabolism might be relevant to other research on how WDR62 cellular and molecular dynamics are impactful on neural development and malignancies.

Expertise:

Human neural development and alterations, iPSCs, neural stem cells, CRISPR-Cas9

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Referee #2

Evidence, reproducibility and clarity

Summary: The authors provide evidence to reveal the novel functions of WDR62 protein in maintaining the stability and activity of purine metabolic enzymes and overall purine homeostasis. WDR62 interacted with BAG2, and they are recruited to purinosome. WDR62 loss caused accelerated degradation of purine salvage enzyme HPRT, and led to the accumulation of purine nucleotide intermediates.

While this study is compelling and significant for the field of neurodevelopmental disorders including microcephaly and purine metabolism, there are several concerns that should be addressed before publication.

Major comments:

• Although all experiments are conducted using non-neuronal cultured cells, does this phenomenon also occur in neuronal cells?
• What is the interaction between endogenous WDR62 and Bag2? This is because in overexpression systems, multiple chaperones may interact with the target protein during protein folding.
• Is endogenous WDR62 also present in the purinosome in purine depleted or sorbitol condition?
• Regarding Fig6 and Fig7, when HPRT decreases and inosine accumulates in WDR62-KO condition, did the levels of hypoxanthine, xanthine, and uric acid change?
• Does HPRT and the three microcephaly-associated WDR62 mutants also recruited in the purinosome in purine depleted or sorbitol condition?
• In Fig7C, HPRT/tubulin ratio appears to decrease in WT from 0hr to 24h, but the graph does not show this decrease. Additionally, quantification of PFAS(FGAMS) and BAG2/tubulin should be performed.
• Fig7D is problematic. HPRT in WDR62-KO cells seems to localize in the nucleus, possibly due to stronger exposure in KO conditions compared to WT. Also, the line scan is drawn in areas with low signal in WT. The comparison should be performed in areas with high perinuclear signal.
• The localization of HPRT should be compared in WT and WDR62-KO with BAG2 siRNA. It is also possible to confirm whether the phenotypes observed in KO, such as cell proliferation and xanthosine/inosine levels, are rescued.
• It should be considered that the induction of Bag2 in WDR62-KO might allow purinosome formation to proceed normally due to compensation. The co-localization of WDR62 and purine enzymes during purinosome formation should be compared when BAG2 expression is suppressed. Similarly, any changes in BAG2 localization in WDR62-KO should be examined. Furthermore, the purinosome formation ability should be compared in WDR62KO + Bag2 siRNA condition.
• The reduction of HPRT in WDR62-KO should be examined for potential effects of enhanced degradation via the ubiquitin-proteasome system or the autophagy-lysosome system.
• Although it is known that HPRT-KO mice do not exhibit any effects on normal brain development except in some dopaminergic neurons, what are your thoughts on this?

Minor comments:

• Please write the full name before the abbreviation of the gene.
• There is no measurement data for Fig7C, and a measurement line is drawn only in one panel of the ROI.
• The line 488 "Fig11" looks like a typo.
• The table could not be found.
• It is strange that all measurement values for WT or control in Fig2, Fig7, and FigS9 are exactly 1.0 without any variation. Please check the measurement method again.
• Please write the method for purine depleted medium.

Referees cross-commenting

I concur with the accurate point observations by the other reviewers. The authors should address the most of the comments provided, as many of the suggested experiments are feasible. If the paper aims to elucidate the one of the causes of microcephaly, specifically, the issues related to cell type and endogenous proteins experiments need to be resolved, and addressing these issues would substantially enhance its quality and impact.

Significance

Most of the roles of purinosomes in the central nervous system remain unknown. The discovery that the WDR62/MCPH2 gene, responsible for microcephaly, is related to purinosomes will have a major impact on this field. Additionally, the ability to easily induce purinosomes through sorbitol phase separation is a significant technical advance in terms of cost and simplicity. Furthermore, many genes related to microcephaly, such as MCPH, are factors directly involved in cell division by regulating the mitotic spindle and centrosomes. This study has revealed a new role for WDR62, uncovering part of a novel molecular mechanism for microcephaly.

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Referee #1

Evidence, reproducibility and clarity

In Morris, M.J. et al., the authors strive to better understand the roles for the microcephaly protein WDR62 in brain growth and function. To accomplish this, an in situ biotinylation assay was performed and identified 42 proteins proximal to WDR62 including the Hsp70 co-chaperone BAG2. Through a series of co-immunoprecipitation assays, the BAG2-WDR62 interaction was shown to be mediated through the structured N-terminal region of WDR62, and it was proposed that common WDR62 mutations disrupt this interaction. In AD293 cells, loss of WRD62 expression resulted in an increase in the expression of BAG2 expression while reducing HPRT expression. Subsequent loss of BAG2 expression by siRNA treatment restored the expression of HPRT suggesting that there is an association between the stability of HPRT and BAG2, likely mediated through its proposed association with Hsp70/90 molecular chaperones. Finally, the authors investigate the subcellular localization and ability of WRD62 to phase separate. WRD62 was shown to form discrete condensates induced by sorbitol-mediated hyperosmotic stress. The formation of WRD62 granules are hypothesized to be driven by cell volume exclusion and macromolecular crowding. These granules appear similar, both in physical appearance and characteristics, to other reported biomolecular condensates such as those reported in metabolism (e.g. purinosomes). WRD62-containing condensates were shown to colocalize with enzymes in de novo purine biosynthesis; however, this association is not required for purinosome formation and/or its stability under both purine-depleted and sorbitol-driven growth conditions. Overall, the manuscript provided a previously unrealized and exciting association between WDR62 and purine metabolism.

EVIDENCE, REPRODUCIBILITY AND CLARITY

Summary: The current manuscript reads as multiple manuscripts with findings that are at times weakly connected (in my opinion). For example, I had a hard time understanding how the BioID results relate to the discovery of WRD62 phase-separation and its colocalization with purinosomes. I would strongly encourage the authors to consider dividing the results into separate manuscripts to strengthen their claims and create a more focused and cohesive manuscript (or series of manuscripts). I believe then several of my reservations associated with the current manuscript will be addressed, and in my opinion, the hard work from the authors will be better received across the scientific community.

I would like to commend the authors for all the work that went into the current version of the manuscript. Being part of a biochemistry and cell biology research group, I completely understand how much time and effort must have went into generating these data. That being said, I felt that there were several instances where clarification and additional information is warranted to arrive at the conclusions made by the authors. These points are outlined below.

Major Comments:

1. There appears to be a discrepancy between the data presented in Figure 1 and what is stated in the main text. Clarification is necessary to better understand the results:
   • The following statement (and derivatives of it) are repeated throughout the manuscript: "...we found that the WDR62 interactome comprised molecular chaperones such as HSP70, HSP90, and their co-regulators, BAG2, STIP1, and DNAJC7" (lines 91-93, 316-318, 422-425). STIP1 and DNAJC7 were not identified in the list of 42 proximal proteins to WDR62 (Figure 1D). DNAJC7 was included because of a previous report curated in the BioGRID database, and there is no mention of HSP90 in the data produced in Figure 1. Please revise the main text to reflect the data that was generated.
   • Based on the data presented in the Venn Diagrams in Figure 1D, the author's numbers do not seem to be consistent with the sentence on lines 126-128. I count 37 proteins unique to their BioID study, 90 unique to the BioGRID database, and 5 proteins that overlap between the two data sets. This sentence needs to be revised.
   • What data were used to generate the interaction map in Figure 1I? Enzymes tied to purine metabolism were not identified from the data presented in Figure 1D but have now appeared. A discussion of this in the main text is warranted.
2. This reviewer has several reservations on how the various key players in the manuscript are related to substantiate the conclusions made in the manuscript. For instance, how is HPRT, purinosomes, and WDR62 related? How about HSP90, WRD62, and HPRT? Pairwise connections were made throughout the manuscript; however, trying to tie all three together is difficult with the data presented.
   • The authors tried to connect HPRT, purinosomes, and WDR62 with BAG2; however, this study could greatly improve if we understood how a knockdown of BAG2 impacts purinosome formation and/or WDR62 colocalization with purinosome enzymes.
   • Is HPRT a client of HSP90? And how are WRD62 and HSP90 related since they do not associated (based on your BioID data)? These connections would again strengthen the arguments made in the manuscript and help to explain the HSP90 inhibition data presented in Figures 7F and 7G.
3. Caution is warranted when making conclusions about WDR62 (and its granules) and purinosomes.
   • The authors describe the association between WDR62 and purinosomes differently throughout the text. I would recommend that the authors come to some conclusion about this and be consistent.

A. (Lines 339-340) "WDR62 granules represent or overlap substantially with the phase-separated metabolons known as purinosomes". Based on the data presented, it appears that these might still be different entities but either overlap or have similar components. Purinosome localization with mitochondria (approx 60-80%) and microtubules (approx 90-95%) were significantly higher than those reported for WDR62 granules (approx 40%). This comparison would suggest that not all WDR62 granules behave similarly to purinosomes. And from the dot plot in Figure 3G, about half of the characterized WDR62 granules do not align with the previously reported characteristics of purinosomes.

B. In the abstract and introduction, the authors state that WDR62 is being recruited to the purinosome and leave out the other possibility. I would recommend that the authors soften this claim in these sections because of the above possibility but also the lack of characterization of the sorbitol-induced "purinosomes". There is little discussion or evidence for how sorbitol induces purinosome formation. Is de novo purine biosynthesis activated upon sorbitol treatment? Are multiple de novo purine biosynthetic enzymes present in the sorbitol-induced "purinosomes"? Further, I agree that there is a tendency for WDR62 to associate with condensates that bear an enzyme within de novo purine biosynthesis; however many of these proteins are known to self-aggregate upon cell stress. Therefore, the entities that are being observing and called purinosomes might not be bone fide purinosomes. Additional care is necessary to make these statements. In my opinion, the current data only suggests that this might be a possibility.

• (Lines 325-329) The authors reference a previous manuscript demonstrating that co-chaperones co-cluster with purinosomes. Based on this fact, they infer that WDR62 granules might represent purinosomes since WDR62 interacts with these same set of co-chaperones. These co-chaperones interact with a large number of different proteins (in fact, most kinases), so it is uncertain how the authors decided to go down this path to link purine metabolism with WDR62. Discussion of how this connection was made would help elevate the story. What additional insights did they have that lead them down these investigations?
• If WDR62 is not required for purinosome formation, why would it localize with the purinosome? Is there any hypothesis that could be readily tested to better help understand this observation? Providing a better understanding of this would greatly elevate the work.

A. (OPTIONAL) Please validate that the associations between WDR62 and the purine biosynthetic enzymes occur on the endogenous level (void of transient transfection). Many methods such as immunofluorescence and proximity ligation assays have been used by others to demonstrate protein-purinosome interactions. This result would reduce any concern that the association is a result of overexpression (artifact).

B. Figures 6F and 6G conclude that nucleosides from purine-depleted growth conditions accumulate while the corresponding monophosphates do not change between WRD62 knock-out and wildtype cells. Given that purine-depleted growth conditions activate de novo purine biosynthesis (uncertain if this has been demonstrated in AD293 cells), could this result simply demonstrate that purine salvage is no longer used and the nucleosides have accumulated and are awaiting degradation (or exportation) rather than a loss of HPRT expression as inferred from the stated conclusions? The conclusions could be better substantiated with the use of a stable isotope incorporation assay.

Is there a difference in the contribution of de novo purine biosynthesis and purine salvage to the generation of the monophosphates (AMP, GMP) between WDR62 knockout and wildtype AD293 cells? Use of a stable isotope (such as 15N-glutamine) could help to come to the appropriate conclusion.

(Lines 483-485) If there is a change in de novo purine biosynthesis, are there any detectable changes in AICAR levels that might influence purine metabolism at the transcriptional level?

Are the data and the methods presented in such a way that they can be reproduced? Are the experiments adequately replicated and statistical analysis adequate?

1. For purine-depleted studies (metabolite analyses, microscopy), how long were the cells grown in purine-depleted medium before the analysis? And how was the purine-depleted medium generated? Please reference any source that might have been used.
2. Details describing the BioID experiment are minimal. How many replicates were performed, was label-free or TMT quantitation used for the protein identification. Further the data analysis and mining of the proteins from the BioID study are missing - What database was used to identify the proteins from the peptides? Please include this information in the Materials and Methods section as well as a link to a repository where the LC-MS/MS data generated can be found. Additionally, it would be very helpful to have a spreadsheet or table that lists the biotinylated proteins and expectant or p values for each.
3. Please include information about the streptavidin pulldown presented in Figure 1C.
4. Many of the figure legends could benefit from a statistical description.
5. There seems to be only two data points for Figure S3A. While there is no significant difference observed, it would be ideal to have additional replicates.
6. (Figure 5I) Please provide statistical analysis to demonstrate the colocalization between FGAMS and WDR62 is robust in purine-depleted AD293 cells.

Minor Comments:

Do you have suggestions that would help the authors improve the presentation of their ideas and conclusions?

1. The use of HSP90 inhibitors is a little confusing given the connections being made with BAG2 and other HSP70 co-chaperones in Figure 1.
   • Does the same conclusions hold true with an HSP70 inhibitor or siRNA?
   • (OPTIONAL) There are a lot of discrepancies between Hsp90 inhibitors and effective treatment concentrations. For example, NVP-AUY922 caused purinosomes to disassemble whereas STA9090 cause purinosomes to change morphology and adopt a more aggregated state. Do other Hsp90 inhibitors share the same phenotypic response as NVP-AUY922 in this study?
   • The treatment time (24 h) with NVP-AUY922 is very long. Given that Hsp90 interacts with hundreds of proteins, it is hard to understand whether the effect of Hsp90 inhibition is direct or indirect. Shorter times (1 h or less) would be more insightful.
2. (OPTIONAL) Does the 2.6-fold increase in BAG2 increase its association with WDR62?
3. Is the degradation of HPRT occurring through BAG2-mediated proteasomal degradation? Showing HPRT recovery by treating the cells with MG132 along with CHX would provide meaningful clues as to how BAG2 and HPRT might be related - Is BAG2 concentration increasing to facilitate the enhanced degradation of HPRT?
4. Does HPRT colocalize with WDR62 in cells?
5. (OPTIONAL) It would be nice to see validation experiments of some of the hits in Figure 1D or 1E in a co-immunoprecipitation experiment conducted similar to Figure 1C.
6. The authors presented the findings that suggest that BAG2 interacts differently with commonly observed WDR62 mutations in MCPH2? How do these mutations affect WDR62 condensation, colocalization with purinosomes, or alter HPRT activity? Tying back the observations to something clinical would help elevate the overall significance of the findings.

Are the text and figures clear and accurate?

1. There are many times throughout the manuscript that the wrong figure is being referenced. These mistakes caused significant confusion at many times while reviewing the manuscript. Please double check all in-text references to figures. For example, I believe that you meant to use Figure S1C instead of Figure 2E with the statement on lines 183-185. Again, I believe that correct figure reference on line 501 is Figure 7G not Figure 7E.
2. The figure legend on Figure S4 does not match the figure and the main text references. Please verify that the text in the figure legends correspond correctly to the figure.
3. Please provide this data for the sentence on lines 399-400 in the supplemental file.
4. I believe that the authors use the phrase "cell proliferation" to describe cell viability in the main text. In the Materials and Methods section, the authors state "The XTT cell proliferation assay enables quantification of cellular redox potential, providing a colorimetric readout of cell viability." Cell proliferation, viability, and cytotoxicity are different measurements, so please revise to reflect the correct experiment that was performed.

Other Minor Comments:

1. Move the sentence "In contrast, despite reduced mRNA..." (lines 387-388) to the last section when a reduction in PFAS expression was first mentioned.
2. Please reference the following in the manuscript:
   • BioGRID database in the main text and Materials and Methods section
   • The reported study showing the DNAJC7-WDR62 interaction (as curated from BioGRID)
   • Fiji in the Materials and Methods section
3. (Line 461-463) The authors state the following: "the loss of WDR62 leads to an increase in BAG2 and vice-versa (Fig. 7A) (Fig. S9B). I am not sure that the vice-versa (i.e. loss of BAG2 increases WDR62) is true. From the data presented in Figure 7H, I do not see a significant change in WDR62 expression upon BAG2 siRNA treatment.
4. For your BioID study, do you know how many or the proportion of cells that were mitotically arrested with the low dose of nocodazole (200 ng/mL)? Given the small number of unique proteins that were in the mitotic only population, it is curious to know how enriched the cells were and whether WDR62 localization is important in the context of this study.
5. Just to clarify, the WDR62-HA lane (third in each set) in Figure 1C is not WDR62-BirA*-HA and that it is only being used as a control.
6. In the Discussion (lines 439-441) "We also show that WDR62 forms dynamic, phase-separated granules that co-localise with chaperones and purine metabolic enzymes, resembling purinosomes." I believe that the authors meant to say co-chaperones instead of chaperones given no microscopy data was presented showing the colocalization of HSP70/90 with WDR62 granules. Please revise.

Referees cross-commenting

I agree with the comments and recommendations by the other reviewers. Many of our shared comments are those that need to be addressed to substantiate the claims made by the authors throughout the manuscript. The proposed experiments across the reviewer comments appear feasible given that similar experiments have already been presented in this version of the manuscript. I strongly encourage the authors to consider these comments when revising their manuscript to help strengthen their claims and boost its overall significance and impact.

Significance

Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. Place the work in the context of the existing literature (provide references, where appropriate).

The work presented explains a previously unknown role for WDR62 in the regulation of purine metabolism. Despite all the hard work that was performed to reach their conclusions, the use of the AD293 cell line and the lack of correlating the common WDR62 disease-promoting mutations to the observed findings throughout the entire manuscript slightly reduced my enthusiasm for this work. The presented study leverages a lot of existing literature to establish connections between WR62, co-chaperones, and purine metabolic enzymes, with an emphasis on purinosome metabolon, a condensate comprised of the enzymes in de novo purine biosynthesis.

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

The audience that might be interested in the reported findings would likely be those tied to biomolecular condensates in cellular metabolism and their connection to disease. I also feel that researchers that study microcephaly might be interested in this work. In my opinion, I believe that a broader readership could happen if additional studies were performed to make stronger connections between studies presented.

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.

My field of expertise is tied to understanding the regulation of cellular metabolism through the use of biochemical and biophysical techniques. I am not as familiar with the in depth details of proteomic analysis such as those required for accurate reporting of data tied to protein proximity labeling (BioID) methods.

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Reply to the reviewers

1. General Statements [optional]

The authors wish to thank the reviewers for fair and constructive comments and Review Commons for facilitating the process.

2. Point-by-point description of the revisions

Point-by-point replies to reviewers' comments on the original submitted manuscript are below. Authors' responses are in plain font.

Reviewers' comments:

Reviewer #1

(Evidence, reproducibility and clarity (Required)):

Summary: The authors identify cancer-associated ERBB4 mutations that are selected for functional characterization. Utilizing the BaF3 and MCF10A models, the authors investigate the potential oncogenic role for 11 recurrent ERBB4 mutations. Three mutants (S303F, E452K and L798R) were strongly transforming with the ability to transform both cell models, S303F being unique in its ability to transform both models in the absence of NRG-1. The authors perform modeling to decipher potential mechanisms of action of the ERBB4 S303F, E452K and L798R mutations. The authors assess the ability of HER3 mutations to dimerize with other HER family members and demonstrate that ERBB4 S303F can mediate its activating functions by stabilizing homo- and heterodimers with other ERBB receptors and that the heterodimerization is likely cell/tissue context dependent. The authors demonstrate that transforming ERBB4 mutants are sensitive to pan-ERBB inhibitors and drive resistance to EGFR-targeted therapy in EGFR-mutant NSCLC cells.

Major comments:

Patient data analysis is performed in more than 15 months ago in January 2024. This analysis should be updated.

We thank the reviewer for pointing out the aspect of constantly expanding mutation data in clinical cancer sample databases. We reanalyzed the patient data in cBioPortal (data download 02 May 2025). In this new analysis, the distribution of mutations in ERBB4 did not change (Reviewer only Fig. 1A), and the 18 selected mutations were still the most recurrently mutated ERBB4 mutations (Reviewer only Fig. 1B). Reanalysis of updated patient data did not change the initial rationale of the study, or the conclusions in the submitted manuscript.

Reviewer only Figure 1. Comparison of patient data derived from cBioPortal on January 2024 (01/2024) or May 2025 (05/2025). A) Figure 1B of the original submitted manuscript. B) Supplementary Figure S1C of the original submitted manuscript.

The rationale for selecting the mutations to be studied is not entirely clear. There are no references to support studying mutations in Fig 1B red boxes.

We apologize for not being sufficiently clear on our rationale for selecting the mutations for analysis. The spectrum of mutations across the ERBB4 gene do not demonstrate clear hotspots as seen in for example EGFR, KRAS, or BRAF. However, we observed that there are regions (not necessarily individual amino acid changes) in ERBB4 that seem to accumulate more mutations than other regions. Looking more closely, we observed that these "hot regions" tend to be located in areas where activating mutations have been described for other oncogenic ERBB family members and/or target structurally important regions for receptor activation such as dimerization interfaces. We hypothesized that these characteristics would suggest functional relevance for the mutations in these "hot regions". In the revised manuscript (on page 11), we have revised the text describing the selection of mutations for further analysis, and added references to justify our selection:

"While the missense mutations were distributed across the 1,308 amino acid sequence of ERBB4, lacking obvious hotspot mutations such as observed for example in EGFR or KRAS, clusters of recurrent mutations could be identified (Fig. 1B). These clusters tended to be located in specific regions that are targeted by activating mutations in other oncogenic ERBB family members (Greulich et al., 2005, 2012; Lee et al., 2006; Bose et al., 2013; Jaiswal et al., 2013)and/or are important for receptor activation (Ferguson et al., 2003; Bouyain et al., 2005; Liu et al., 2012), suggesting functional relevance (red boxes in Fig. 1B). Some recurrent mutations were located in the unstructured C-terminal tail of ERBB4 (Fig. 1B). We selected in total 18 ERBB4 missense mutations (indicated in Fig. 1B) that were recurrent and/or located in the abovementioned regions of interest for functional characterization (indicated in Fig. 1B and Supplementary Fig. S1C) - hypothesizing that these mutations would be actionable. Of the different mutants at the same position of ERBB4 amino acid sequence, the most recurrent amino acid change was selected for characterization."

Cell proliferation should be shown for BaF3 cells for continuity in Figure 2 instead of doubling time.

We agree that it may cause confusion that the results for the Ba/F3 and MCF10a experiments in Fig. 2C and D (Fig. 2D and E in the revised manuscript) are reported using a different metric. The reason for this is that these assays measure different outputs: in the Ba/F3 assay, the emergence of proliferating cells under IL3 deprivation is measured, with repeated cell viability measurements over time. In the MCF10a experiment, the ability of ERBB4 mutations to sustain the proliferation of MCF10a cells in the absence of EGF is measured, using a fixed time point (8 days). Thus, doubling time, as an indicator for the time required for the emergence of proliferating cells, is more suitable metric to quantify the relative transforming capability of the different ERBB4 mutations in the Ba/F3 cells. In the case of MCF10a cells, the relevant metric is the cell viability (as a surrogate marker for the number of cells) at the endpoint measurement.

The relative expression of HER3 constructs must be shown for BaF3 and MCF10A cells in Figure 2.

We assume the reviewer is asking to demonstrate the expression levels of different ERBB4 mutants in the Ba/F3 and MCF10a cells used in experiments in Fig. 2C and D (Fig. 2D and E in the revised manuscript). We would like to thank the reviewer for this very relevant point. Western blots demonstrating the expression levels of different ERBB4 mutants in the Ba/F3 and MCF10a cells have now been added as a data new panel in the Figure 2 (Fig. 2B in the revised manuscript). No ERBB3 expression constructs were introduced into the cells.

Blots in Figure 4 must be quantified.

The blots in Figure 4 have now been quantified, and the relative signal intensities are shown below each blot. We thank the reviewer for suggesting this relevant analysis. The analysis revealed two issues that we have now revised:

1) in Fig. 4D, the dimerization of EGFR with ERBB4 S303F is not convincingly increased when compared to EGFR dimerization with wild-type ERBB4. Therefore, we have omitted that conclusion from the results section:

"Taking into account these expression level differences, ERBB4 S303F did indeed co-immunoprecipitate more efficiently than wild-type ERBB4 with ERBB2 and EGFR both in the presence or absence of NRG-1 (Fig. 4D), demonstrating that the S303F mutation promotes the formation of ERBB heterodimers."

Omitting this data does not change our final conclusion, that the ERBB4 S303F mutation leads to enhanced ERBB4 heterodimerization.

2) In Fig. 4C, the previously published ERBB4 D595V mutant, used as a control in the experiment, does not clearly demonstrate enhanced ERBB4 homodimerization after quantifying the blots. Therefore, we have cropped the lanes representing the ERBB4 D595V mutant from the blot, and omitted the part of the results text that discusses this ERBB4 mutant:

"ERBB4 homodimers were assessed by crosslinking cell surface proteins with a cell membrane impermeable BS3, enabling detection of ERBB4 dimers as high molecular weight species of ERBB4 in western blot. Another activating extracellular ERBB4 mutation, D595V, was used as a positive control, as we have previously demonstrated D595V to stabilize ERBB4 dimers using the same assay (Kurppa et al., 2016). As predicted by the structural analyses, S303F resulted in more abundant active, phosphorylated ERBB4 dimers than wild-type ERBB4 in the presence of NRG-1, while the activating intracellular domain mutation L798R, that served as a negative control for dimer stabilization, did not (Fig. 4C)."

Omitting these data does not change our final conclusion, that the ERBB4 S303F mutation leads to enhanced ERBB4 homodimerization.

There are major concerns with Supplemental files. It is imperative that the effectiveness of HER3 shRNA be shown in S Fig3. These data are not interpretable without this.

We apologize for confusion related to the supplemental files. The effectiveness of the ERBB3 (HER3) shRNA is shown in the Supplementary Figure S3B of the original submitted manuscript.

Lanes in S Fig 4 are not marked again making data not interpretable.

Some of the lanes in the Supplementary Figure 4B were not marked because the experiment contained other ERBB4 constructs in addition to the ones that are marked and discussed in the manuscript text. The reason for leaving the unmarked lanes in the final figure was to emphasize that the bands indicated come from the same membrane, blot and exposure. We understand how this may cause confusion, and thus have now cropped the blots to include only the lanes discussed in the manuscript text.

It's unclear why Table 1 is included as this is already published data. This previously published data should be summarized in the text.

We are happy to elaborate the novelty of the data in Table 1 of the original submitted manuscript. The data is from the SUMMIT trial (NCT01953926) (Hyman et al., 2018), the results of which have been published. However, the three patients in the top part of the table were enrolled to the SUMMIT trial based on the ERBB4mutation in their tumor, and the data for these patients have not previously been published. We received these data directly from Puma Biotechnology. In addition, while the ERBB4 mutation status for the patients in the lower part of the table has been published in the supplementary files of the Hyman and others publication, we feel that the patients' ERBB4 mutations merit discussion, and including these patient data in the table would complement the data on the three patients in the top part of the table. Due to these reasons, we feel that the table contains unpublished and relevant data for the study, and would like to keep the table in the manuscript by moving it into the Supplementary Data (Supplementary Table S2).

To clarify the sources of the patient data, we have modified the methods section related to the table as follows:

"Neratinib efficacy data, cancer types and co-alterations of patients harboring an ERBB4 alteration, enrolled in PUMA-NER-5201, the SUMMIT trial (NCT01953926), and treated with neratinib as a single agent (240 mg/day) were obtained from Puma Biotechnology (for patients enrolled based on an ERBB4 mutation - previously unpublished data) and cBioPortal (for patients with ERBB4 as a co-altered gene, enrolled based on an ERBB2 or ERBB3 mutation)."

This text is now moved to "Supplementary Methods" under a new section "Neratinib efficacy in patients" on page 9 of the revised Supplementary Data -file

There is a disconnect why the last two figures focus on a single model of NSCLC whereas the three most transforming mutations are found most commonly in breast, melanoma and GI tract cancers.

The reviewer is correct in that the most transforming ERBB4 mutations are indeed found most commonly in beast and esophagogastric cancers and in melanoma. However, in the context of targeted therapy resistance,mutations that confer resistance are often acquired during therapy, and may not represent the typical cancer type-specific mutational patterns. The strongest evidence for a potential role of mutant ERBB4 in therapy resistance comes from the context of EGFR-targeted therapies and lung cancer. As mentioned in the results and discussion sections of the submitted manuscript, ERBB4 mutations identified in patients who developed resistance to EGFR-targeted therapy (Cremolini et al., 2019; Jänne et al., 2022), include the same mutation or mutation in the same residue as analyzed in the current study: the strongly transforming S303F or L798I. In addition, a recent study showed that EGFR-mutant lung cancer patients with co-occurring ERBB4 mutations have shorter relapse-free survival on osimertinib treatment (Vokes et al., 2022). Therefore, we focused on EGFR-mutant lung cancer as the model system to assess, as proof-of-concept, whether activating, transforming ERBB4 mutations are able to confer resistance to EGFR-targeted therapy. To make the transition to cancer therapy resistance and the rationale for choosing the model context more clear, we have added text to the start of the "Activating ERBB4 mutations drive resistance to EGFR-targeted therapy in EGFR-mutant NSCLC cells" -chapter of the revised manuscript:

"There is emerging evidence associating ERBB4 with cancer therapy resistance across various cancer types and treatment regimens (Merimsky et al., 2001, 2002; Mendoza-Naranjo et al., 2013; Nafi et al., 2014; Saglam et al., 2017; Wege et al., 2018; Wang et al., 2019; Zhang et al., 2023; Debets et al., 2023; Albert et al., 2024; Arribas et al., 2024), including ERBB4 mutations that have been found in patient tumors after acquisition of therapy resistance (Cremolini et al., 2019; Jänne et al., 2022; Vokes et al., 2022; Yaeger et al., 2023; Yuan et al., 2023). Intriguingly, the ERBB4 mutations identified in patients who developed resistance to EGFR-targeted therapy (Cremolini et al., 2019; Jänne et al., 2022), include the same mutation or mutation in the same residue as analyzed in the current study: the strongly transforming S303F or L798I. In addition, co-occurring ERBB4 mutations in EGFR-mutant lung cancer patients have been shown to associate with shorter progression-free survival on EGFR inhibitor therapy (Vokes et al., 2022). These observations point to the possibility that mutant ERBB4 could promote resistance to targeted therapies."

What are the differences in the recurrent ERBB4 mutant tumors versus ERBB4 wild-type tumors described in Figure 7?

The reviewer points out a very relevant question. We suspect that in the tumors expressing mutant ERBB4, the activating ERBB4 mutants are able to compensate for the loss of EGFR signaling, particularly since the on-treatment cancer cells demonstrate elevated levels of ERBB4 ligands (Fig. 7C, D). This is analogous to accumulating evidence suggesting that ERBB4 independently and together with ERBB3 (and/or with increased availability of their ligands) compensate for survival and growth signaling upon ERBB2- or EGFR-targeted therapy (Carrión-Salip et al., 2012; Wilson et al., 2012; Nafi et al., 2014; Canfield et al., 2015; Yonesaka et al., 2015; Donoghue et al., 2018; Shi et al., 2018; Debets et al., 2023; Udagawa et al., 2023). Unfortunately, we are unable to approach this hypothesis using samples from the in vivo experiment in Fig.7. The treatment of the mice was stopped after 189 days of treatment in order to assess how many tumors grew back (i.e. how many mice were cured by the treatment). For this reason, we do not have the appropriate controls to analyze ERBB4 mutant-associated changes in on-treatment tumors.

Figure 7C, D should be moved to supplemental as this is from previously published data and not strictly relevant to data shown in Fig 7.

The data shown in Fig. 7C and D are a re-analysis of published single-cell RNA-seq data. While the single cell RNA-sequencing data set is previously published, the analysis of ERBB4 ligand expression performed, and shown in Fig. 7C and D has not been published before. We feel that these data provide evidence of a previously unrecognized upregulation of ERBB4 ligand expression in on-treatment EGFR-mutant NSCLC cells in vivo. Furthermore, as discussed in the results section of the original submitted manuscript (page 26; page 28 of the revised manuscript), the upregulation of ERBB4 ligands in the on-treatment tumors provides a plausible mechanism supporting mutant ERBB4 activation upon EGFR inhibitor treatment, as the transforming ERBB4 mutants seem to retain at least partly the dependency of ligand stimulation. Thus, we feel that these data are unpublished and relevant for the manuscript, and we would like to keep these data panels in the main Figure 7.

Limitations should include consideration of endogenous levels of ERBB4 in the model systems used and disparate expression levels of wt ERBB4 versus ERBB4 mutation.

We thank the reviewer for pointing out that we have not thoroughly disclosed the endogenous levels of ERBB4 expression in the used model systems. None of the used model systems (MCF10a, Ba/F3, COS-7, PC-9) express detectable levels of ERBB4 protein. This was mentioned in the original submitted manuscript for COS-7 (page 19; page 20 of the revised manuscript), Ba/F3 cells (page 18; page 19 of the revised manuscript), and PC-9 cells (page 24; page 24 of the revised manuscript), but not for MCF10a cells. We have now made this point more clear, and added a sentence "Neither of these models express detectable levels of ERBB4" in the results section under the chapter "Majority of the recurrent ERBB4 mutations are transforming in Ba/F3 or MCF10a cells" (page 12-13 of the revised manuscript), as well as to the discussion section (page 30 of the revised manuscript).

Regarding the expression levels of different ERBB4 mutants versus ERBB4 wild-type, we have now added the new Figure 2B, showing the expression of all ERBB4 mutants and ERBB4 wild-type in Ba/F3 and MCF10a cells. We have also included the following text describing the expression levels of ERBB4 mutants in the results section under "Majority of the recurrent ERBB4 mutations are transforming in Ba/F3 or MCF10a cells" (page 13 of the revised manuscript):

"The different ERBB4 mutants demonstrated similar expression levels compared to wild-type ERBB4 in both model systems with the exception of R106C and G907E mutants that were expressed predominantly as immature receptor forms in both models, suggesting defective receptor maturation. Also, the R1304W mutant demonstrated lower expression levels in the Ba/F3 cells, and could not be expressed at all in the MCF10a cells (Fig. 2B)."

Minor comments:

Fig1B lists ERBB3 V104V mutation?

Thank you for noticing this mistake. This has now been corrected in the revised Figure 1B.

List frequency of ERBB4 mutations in the introduction

We thank the reviewer for the suggestion and have revised the introduction to include an example of the high frequency of ERBB4 missense mutations in cancer as follows:

"Yet, despite the high frequency of ERBB4 missense mutations in various cancer types (up to 30% in non-melanoma skin cancer, Supplementary Fig. S1A, B) and characterization of several potentially oncogenic ERBB4 mutations (Prickett et al. 2009; Nakamura et al. 2016; Chakroborty et al. 2022; Kurppa et al. 2016; Tvorogov et al. 2009), the rationale for clinically targeting ERBB4 in cancer has not been fully developed."

Clarification throughout if cells are serum-starved (how long) if stimulated with NRG-1

We thank the reviewer for the thoughtful suggestion and have revised the main text and figure legends accordingly; in the revised manuscript on pages 6, 8, 9, 13, 17, 20, 25 and 26 "(10% serum)", on page 25 "following short-term stimulation with NRG-1 after overnight serum starvation (Fig. 6A).", as well as figure legends of Fig. 2, 4, 5, 6, S2, and S3.

Reviewer #1 (Significance (Required)):

General assessment: This work fills a gap in cancer research understanding if ERBB4 mutations could be targeted. Concerns and comments need to be addressed before definitive conclusions can be made.

The authors wish to thank the reviewer for the positive assessment.

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Reviewer #2

(Evidence, reproducibility and clarity (Required)):

Ojala et al. report a very extensive exploration of the functional relevance of somatic mutations occurring in the ERBB4 gene. The Authors demonstrate that 11 out of 18 mutations they studied have oncogenic potential, with some of them actionable using clinically available ERBB inhibitors, while giving resistance to EGFR inhibitors.

A very minor comment. At the beginning of page 21, I'd not define PD as the best respone. The Authors can write that all four patients progressed under treatment.

We would like to thank the reviewer for the comment. We agree with the reviewer, and have now revised the sentence in question as follows:

"Two of the three patients that were qualified for the SUMMIT trial due to a mutation in ERBB4, with no other qualifying mutations in ERBB family genes, had an ERBB4 mutation characterized in this study to be transforming (R544W and V840I) (Supplementary Table S2). Yet, neither of these patients, nor the patient with an ERBB4 VUS N465K, responded to neratinib and progressed under treatment (Supplementary Table S2)."

Reviewer #2 (Significance (Required)):

The work by Ojala et al. is the most detailed study of mutations occurring in ERBB4. Since these are relatively rare, they have not been properly studied up to now. The study is very well done.

The authors wish to thank the reviewer for the very positive statement.

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Reviewer #3

(Evidence, reproducibility and clarity (Required)):

Summary - This work has mined cBioPortal to identify candidate cancer driver mutations in the gene encoding the ERBB4 receptor tyrosine kinase (Figure 1). These ERBB4 mutations occurred in clusters that are paralogous to activating mutations in other ERBB receptor genes or in clusters predicted to serve as dimerization interfaces of ERBB4. Eighteen such ERBB4 mutations were selected for characterization.

• These mutants were tested in BaF3 and MCF-10A cells in the context of the ERBB4 JM-a CYT-2 isoform (Figure 2). Several of these ERBB4 mutants exhibited greater agonist-dependent coupling to cell proliferation than wild-type ERBB4. Moreover, some of the mutants exhibited greater agonist-independent coupling to cell proliferation than wild-type ERBB4. Five ERBB4 mutants (S303F, E452K, L798R, R992C, S1289A) exhibited greater activity in the BaF3 cells, whereas nine ERBB4 mutants (S303F, R393W, E452K, R544W, R711C, S774G, L798R, V840I, G870R) exhibited greater activity in the MCF10A cells. Thus, eleven of the ERBB4 mutants (S303F, R393W, E452K, R544W, R711C, S774G, L798R, V840I, G870R, R992C, S1289A) exhibited a gain-of-function phenotype. It should be noted that several of the ERBB4 gain-of-function mutants (R393W, R544W, R711C, V840I, G870R, R992C, S1289A) exhibited cell type specificity.

• PyMol was used to "model" the effect of the most potent (S303F, E452K, and L798R) gain-of-function mutations on the structure of ERBB4 (Figure 3). These three mutations are predicted to cause increased ERBB4 dimerization.

• When expressed in MCF-10A cells, the most potent (S303F, E452K, and L798R) gain-of-function ERBB4 mutants exhibited elevated ligand-dependent and ligand-independent tyrosine phosphorylation. This was accompanied by elevated EGFR, ERBB2, and ERBB4 tyrosine phosphorylation and elevated signaling by canonical effector proteins (Figure 4).

• The homo- and heterodimerization of the most potent ERBB4 mutant (S303F) was studied following transient transfection of COS-7 cells (Figure 4). As predicted, the S303F mutant exhibited greater ERBB4 homodimerization and greater heterodimerization with EGFR and ERBB2, but not with ERBB3.

• The data from the clinical trial NCT01953926 was mined to evaluate whether the presence of an ERBB4 activating mutation found in this work is associated with sensitivity to the pan-ERBB inhibitor neratinib (Table 1). Surprisingly, a compelling association was NOT found. In contrast, the proliferation of BaF3 cells that express gain-of-function ERBB4 mutants is sensitive to the irreversible pan-ERBB inhibitors neratinib, afatinib, and dacomitinib (Figure 5).

• Mining the cBioPortal, AACR GENIE, and COSMIC datasets indicates that the three most potent ERBB4 gain-of-function mutants (S303F, E452K, and L798R) exhibit tissue specificity (Supplementary Figure S5). Moreover, the S303F mutation is coincident with a mutation in another ERBB receptor to a much lesser degree than other gain-of-function ERBB4 mutants, particularly E452K. This too is suggestive of differences in the mechanism of action among the gain-of-function ERBB4 mutants (Supplementary Figure S5).

• To test the effect of ERBB4 gain-of-function mutants on resistance to EGFR inhibitors, PC-9 NSCLC cells (which contain an endogenous gain-of-function EGFR mutant but do not endogenously express ERBB4) were transduced with ERBB4 gain-of-function mutants. In these cells the S303F and L715K mutants exhibited elevated ERBB4 signaling, but the L798R and K935I mutants did not. Nonetheless, the S303F, E715K, and K935I mutants promoted osimertinib resistance upon long-term treatment in vitro, whereas the L798R mutant did not (Figure 6). Moreover, the E715K and S303F mutants caused osimertinib resistance in vivo.

• Overall, this is an impressive body of work. The experiments have been carefully performed and the data are clearly presented. However, the breadth of this work makes it a bit unfocused and difficult to digest.

The authors wish to thank the reviewer for the positive statement.

Major Issues Affecting the Conclusions

The COS-7 data in Figure 4 are probably generated using supraphysiological levels of ERBB4 expression, raising concerns about the ability to draw general conclusions from these data. This issue should be addressed.

We appreciate the reviewer's insight on the details concerning experimentation in COS-7 cells. We acknowledge the drawbacks in experiments performed using transient overexpression of proteins in COS-7 cells using vectors with strong viral promoters. To mitigate these drawbacks, we routinely perform transient overexpression in COS-7 cells using the retroviral pBABE-vectors, which have a weak promoter and produce relatively moderate protein expression level. We have included here a reviewer-only figure (Reviewer-only Figure 2) that demonstrates the ERBB4 expression level derived from the pBABE-vector, compared to endogenous expression level of ERBB4 in T47D and MCF7 cells, as well as to ERBB4 expression derived from pcDNA3.1 vector that harbors a strong viral CMV promoter. With this, we hope to convince the reviewer that the ERBB4 expression levels in our COS-7 cell experiments are not supraphysiological.

Reviewer-only Figure 2. The expression level of ERBB4 in T47D and MCF7 cells, as well as in COS-7 cells transiently transfected with equal amounts of pBABE-puro-gateway-ERBB4JM-aCYT-2 plasmid, or pcDNA3.1.-ERBB4JM-aCYT-2 plasmid.

The inhibitor data shown in Figure 5 may be over-interpreted. The affinity of neratinib, afatinib, and dacomitinib for EGFR is reportedly higher than the affinity of these drugs for ERBB4. Thus, the failure of ERBB4 gain-of-function mutants to cause resistance to these inhibitors may be because the inhibitors bind to endogenous EGFR and therefore fail to bind to ERBB4.

We thank the reviewer for the insightful comments. The experiments in Figure 5 were performed in Ba/F3 cells, which do not express endogenous EGFR, or other kinase competent ERBB receptors (Riese et al., 1995). Therefore, it is unlikely that the observed cellular responses to neratinib, afatinib, or dacomitinib are affected by the drugs' preferable binding to EGFR.

Moreover, the conclusion that the gain-of-function ERBB4 mutants are targetable with these inhibitors appears to be an overreach.

We have revised our conclusion into that ERBB4 mutants are "sensitive to" these inhibitors, as supported by our data in Figure 5. This revision has been made in the abstract (page 2), introduction section (page 4), results section (page 23), and in the discussion (page 31) of the revised manuscript.

The inhibitor data shown in Figure 6 demonstrates that activating ERBB4 mutations are sufficient to drive inhibitor resistance. However, these data do not demonstrate that the mutations are necessary to drive inhibitor resistance. Thus, these data are of less value than represented in this work. Knockout or silencing (CRISPR or siRNA) experiments would be more definitive.

We agree with the reviewer that performing knock-out or silencing experiments to demonstrate the necessity of mutant ERBB4 for inhibitor resistance would strengthen the conclusions. However, the PC-9 cells (or any other EGFR-mutant NSCLC cell lines) do not express endogenous ERBB4, and do not have endogenous ERBB4 mutations. Therefore, knock-out or silencing experiments are unfortunately not possible in this setting.

Minor Issues That Can Confidently Be Addressed

In Figure 2, the MCF10A data are more compelling than the BaF3 data. Thus, an argument can be made that the BaF3 data belong in a supplemental figure. However, the combination of data from both cell lines illustrate the fact that ERBB4 mutants appear to exhibit cell type specificity. If this point is emphasized in the text, then Figure 2 should remain as currently presented.

We agree with the reviewer that our data suggest that the ERBB4 mutants demonstrate a level of context-specificity. This was mentioned in the results section of the original submitted manuscript (page 20; page 21 of the revised manuscript) as well as discussed in the discussion section (page 29; page 29 of the revised manuscript). To emphasize this further, we have revised our conclusions at the end of the "Majority of the recurrent ERBB4 mutations are transforming in Ba/F3 or MCF10a cells" -section as follows:

"Taken together, these analyses indicate a potential oncogenic role for 11 recurrent ERBB4 mutations. Eight of the mutations were transforming in only one of the models used, suggesting context-specificity. Three mutants (S303F, E452K and L798R) were strongly transforming with the ability to transform both cell models, S303F being unique in its ability to transform both models in the absence of NRG-1."

The modeling data shown in Figure 3 are a bit under-interpreted. It would appear that the S303F, E452K, and L798R mutants would cause increased ERBB4 signaling by (1) shifting the equilibrium of ERBB4 monomers between the tethered (inactive) state and the extended (active) state or by (2) directly fostering receptor dimerization. The modeling data should be interpreted in the context of these two paradigms.

We thank the reviewer again for an insightful observation. We have now revised the text describing the modeling data based on the reviewer's suggestions (please see the revised manuscript, under "Structural analysis of the transforming ERBB4 mutations").

The mechanistic data shown in Figure 4 are also a bit under-interpreted. The data from Figure 2 suggest that ERBB4 gain-of-function mutants are more likely to promote ERBB4 heterodimerization than ERBB4 homodimerization. Do the data from Figure 4 support this hypothesis?

The authors agree with the reviewer in that the activating ERBB4 mutations lead to increased activation of other ERBB family members (Fig. 4A), supporting a hypothesis that activating ERBB4 mutations lead to increased heterodimerization. We have discussed this throughout the original submitted manuscript, for example making these conclusions:

Results section, page 16 (page 18 of the revised manuscript): "In summary, these data indicate that S303F, E452K and L798R are activating, gain-of-function ERBB4 mutations that may co-operate with other ERBB receptors in malignant transformation.", page 19 (page 20 of the revised manuscript): "Together, these data suggest that while ERBB4 can be transforming in the absence of other ERBB receptors, mutant ERBB4 co-operates with ERBB3 to promote ligand-independent cell transformation.".

Discussion section, page 30 (page 31 of the revised manuscript: "Together, these findings imply that ERBB4 heterodimers with other ERBB receptors can contribute to cell transformation and growth, supporting the rationale for pan-ERBB inhibition approach in targeting mutant ERBB4 in cancer."

Reviewer #3 (Significance (Required)):

General Assessment: Strengths and Limitations

• This work makes a significant contribution to the hypothesis that ERBB4 gain-of-function mutants drive multiple human malignancies. However, this work dances around two issues. (1) Is heterodimerization of EGFR or ERBB2 with ERBB4 required for the transforming activity of these ERBB4 mutants? (2) Are these ERBB4 mutants found in the context of the JM-a/CYT-2 isoform or some other isoform? Are these ERBB4 mutants active in the context of isoforms other than JM-a/CYT-2?

We thank the reviewer for the very positive assessment and insight on specific ERBB4 biology that could affect the functional effect of mutations in ERBB4. We would like to comment on these insights:

1) Since the strongly transforming ERBB mutations all promoted the activation of EGFR, ERBB2, and ERBB3 (Fig. 4A), it is possible that heterodimerization plays a role in the transforming activity of these ERBB4 mutants. However, our data suggests that EGFR and ERBB2 are not necessary for transformation, since the Ba/F3 cells, where transformation by ERBB4 mutants was observed (Fig. 2D), do not express EGFR or ERBB2. We did see a consistent upregulation of endogenous ERBB3 upon IL3 deprivation in the ERBB4 S303F -expressing Ba/F3 cells (Fig. 4B), which contributed to the ERBB4 S303F -driven, IL3-independent transformation (Supplementary Fig. S3C-D).

2) None of the analyzed ERBB4 mutations are located in the JM- or CYT-regions of ERBB4, and thus could hypothetically be expressed in the context of any of the four ERBB4 isoforms. However, cancer tissues almost exclusively express the JM-a isoforms of ERBB4, with roughly similar ratios of CYT-1 and CYT-2 isoforms. We chose to use the JM-a CYT-2 isoform in this study, based on our previous work that has implicated the JM-a CYT-2 isoform as being more oncogenic than JM-a CYT-1 isoform, as elaborated in the original submitted manuscript: "The ERBB4 JM-a CYT-2 isoform was used in the studies based on previous findings suggesting that JM-a CYT-2 is the more oncogenic ERBB4 isoform of the cancer-associated isoforms (Veikkolainen et al., 2011) in hematopoietic cell contexts (relevant for the Ba/F3 cell model) (Määttä et al., 2006; Chakroborty et al., 2022)". We do agree with the reviewer that future studies should determine the relative contribution of JM-a CYT-1 and JM-a CYT-2 isoforms in the ability of mutant ERBB4 to drive cancer growth.

Advance: How Does This Work Advance the Field

• This work will undoubtedly reinvigorate the ERBB4 field.

Audience:

• Those with an interest in the role that ERBB receptors play in human tumors.

My Expertise:

• 30+ years of experience studying ERBB receptors.

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Wilson, T. R. et al. (2012) 'Widespread potential for growth-factor-driven resistance to anticancer kinase inhibitors', Nature. Nature Publishing Group, 487(7408), pp. 505-509. doi: 10.1038/nature11249.

Yaeger, R. et al. (2023) 'Molecular Characterization of Acquired Resistance to KRASG12C-EGFR Inhibition in Colorectal Cancer', Cancer Discovery, 13(1), pp. 41-55. doi: 10.1158/2159-8290.CD-22-0405.

Yonesaka, K. et al. (2015) 'The pan-HER family tyrosine kinase inhibitor afatinib overcomes HER3 ligand heregulin-mediated resistance to EGFR inhibitors in non-small cell lung cancer.', Oncotarget. Oncotarget, 6(32), pp. 33602-11. doi: 10.18632/oncotarget.5286.

Yuan, S. Q. et al. (2023) 'Residual circulating tumor DNA after adjuvant chemotherapy effectively predicts recurrence of stage II-III gastric cancer', Cancer Communications. John Wiley & Sons, Ltd, 43(12), pp. 1312-1325. doi: 10.1002/cac2.12494.

Zhang, J. et al. (2023) 'Tracking of trastuzumab resistance in patients with HER2-positive metastatic gastric cancer by CTC liquid biopsy.', American journal of cancer research. e-Century Publishing Corporation, 13(11), pp. 5684-5697. Available at: http://www.ncbi.nlm.nih.gov/pubmed/38058840 (Accessed: 16 April 2024).

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Referee #3

Evidence, reproducibility and clarity

Summary

• This work has mined cBioPortal to identify candidate cancer driver mutations in the gene encoding the ERBB4 receptor tyrosine kinase (Figure 1). These ERBB4 mutations occurred in clusters that are paralogous to activating mutations in other ERBB receptor genes or in clusters predicted to serve as dimerization interfaces of ERBB4. Eighteen such ERBB4 mutations were selected for characterization.
• These mutants were tested in BaF3 and MCF-10A cells in the context of the ERBB4 JM-a CYT-2 isoform (Figure 2). Several of these ERBB4 mutants exhibited greater agonist-dependent coupling to cell proliferation than wild-type ERBB4. Moreover, some of the mutants exhibited greater agonist-independent coupling to cell proliferation than wild-type ERBB4. Five ERBB4 mutants (S303F, E452K, L798R, R992C, S1289A) exhibited greater activity in the BaF3 cells, whereas nine ERBB4 mutants (S303F, R393W, E452K, R544W, R711C, S774G, L798R, V840I, G870R) exhibited greater activity in the MCF10A cells. Thus, eleven of the ERBB4 mutants (S303F, R393W, E452K, R544W, R711C, S774G, L798R, V840I, G870R, R992C, S1289A) exhibited a gain-of-function phenotype. It should be noted that several of the ERBB4 gain-of-function mutants (R393W, R544W, R711C, V840I, G870R, R992C, S1289A) exhibited cell type specificity.
• PyMol was used to "model" the effect of the most potent (S303F, E452K, and L798R) gain-of-function mutations on the structure of ERBB4 (Figure 3). These three mutations are predicted to cause increased ERBB4 dimerization.
• When expressed in MCF-10A cells, the most potent (S303F, E452K, and L798R) gain-of-function ERBB4 mutants exhibited elevated ligand-dependent and ligand-independent tyrosine phosphorylation. This was accompanied by elevated EGFR, ERBB2, and ERBB4 tyrosine phosphorylation and elevated signaling by canonical effector proteins (Figure 4).
• The homo- and heterodimerization of the most potent ERBB4 mutant (S303F) was studied following transient transfection of COS-7 cells (Figure 4). As predicted, the S303F mutant exhibited greater ERBB4 homodimerization and greater heterodimerization with EGFR and ERBB2, but not with ERBB3.
• The data from the clinical trial NCT01953926 was mined to evaluate whether the presence of an ERBB4 activating mutation found in this work is associated with sensitivity to the pan-ERBB inhibitor neratinib (Table 1). Surprisingly, a compelling association was NOT found. In contrast, the proliferation of BaF3 cells that express gain-of-function ERBB4 mutants is sensitive to the irreversible pan-ERBB inhibitors neratinib, afatinib, and dacomitinib (Figure 5).
• Mining the cBioPortal, AACR GENIE, and COSMIC datasets indicates that the three most potent ERBB4 gain-of-function mutants (S303F, E452K, and L798R) exhibit tissue specificity (Supplementary Figure S5). Moreover, the S303F mutation is coincident with a mutation in another ERBB receptor to a much lesser degree than other gain-of-function ERBB4 mutants, particularly E452K. This too is suggestive of differences in the mechanism of action among the gain-of-function ERBB4 mutants (Supplementary Figure S5).
• To test the effect of ERBB4 gain-of-function mutants on resistance to EGFR inhibitors, PC-9 NSCLC cells (which contain an endogenous gain-of-function EGFR mutant but do not endogenously express ERBB4) were transduced with ERBB4 gain-of-function mutants. In these cells the S303F and L715K mutants exhibited elevated ERBB4 signaling, but the L798R and K935I mutants did not. Nonetheless, the S303F, E715K, and K935I mutants promoted osimertinib resistance upon long-term treatment in vitro, whereas the L798R mutant did not (Figure 6). Moreover, the E715K and S303F mutants caused osimertinib resistance in vivo.
• Overall, this is an impressive body of work. The experiments have been carefully performed and the data are clearly presented. However, the breadth of this work makes it a bit unfocused and difficult to digest.

Major Issues Affecting the Conclusions

• The COS-7 data in Figure 4 are probably generated using supraphysiological levels of ERBB4 expression, raising concerns about the ability to draw general conclusions from these data. This issue should be addressed.
• The inhibitor data shown in Figure 5 may be over-interpreted. The affinity of neratinib, afatinib, and dacomitinib for EGFR is reportedly higher than the affinity of these drugs for ERBB4. Thus, the failure of ERBB4 gain-of-function mutants to cause resistance to these inhibitors may be because the inhibitors bind to endogenous EGFR and therefore fail to bind to ERBB4. Moreover, the conclusion that the gain-of-function ERBB4 mutants are targetable with these inhibitors appears to be an overreach.
• The inhibitor data shown in Figure 6 demonstrates that activating ERBB4 mutations are sufficient to drive inhibitor resistance. However, these data do not demonstrate that the mutations are necessary to drive inhibitor resistance. Thus, these data are of less value than represented in this work. Knockout or silencing (CRISPR or siRNA) experiments would be more definitive.

Minor Issues That Can Confidently Be Addressed

• In Figure 2, the MCF10A data are more compelling than the BaF3 data. Thus, an argument can be made that the BaF3 data belong in a supplemental figure. However, the combination of data from both cell lines illustrate the fact that ERBB4 mutants appear to exhibit cell type specificity. If this point is emphasized in the text, then Figure 2 should remain as currently presented.
• The modeling data shown in Figure 3 are a bit under-interpreted. It would appear that the S303F, E452K, and L798R mutants would cause increased ERBB4 signaling by (1) shifting the equilibrium of ERBB4 monomers between the tethered (inactive) state and the extended (active) state or by (2) directly fostering receptor dimerization. The modeling data should be interpreted in the context of these two paradigms.
• The mechanistic data shown in Figure 4 are also a bit under-interpreted. The data from Figure 2 suggest that ERBB4 gain-of-function mutants are more likely to promote ERBB4 heterodimerization than ERBB4 homodimerization. Do the data from Figure 4 support this hypothesis?

Significance

General Assessment: Strengths and Limitations

This work makes a significant contribution to the hypothesis that ERBB4 gain-of-function mutants drive multiple human malignancies. However, this work dances around two issues. (1) Is heterodimerization of EGFR or ERBB2 with ERBB4 required for the transforming activity of these ERBB4 mutants? (2) Are these ERBB4 mutants found in the context of the JM-a/CYT-2 isoform or some other isoform? Are these ERBB4 mutants active in the context of isoforms other than JM-a/CYT-2?

Advance: How Does This Work Advance the Field

This work will undoubtedly reinvigorate the ERBB4 field.

Audience:

Those with an interest in the role that ERBB receptors play in human tumors.

My Expertise:

30+ years of experience studying ERBB receptors.

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Referee #2

Evidence, reproducibility and clarity

Ojala et al. report a very extensive exploration of the functional relevance of somatic mutations occurring in the ERBB4 gene. The Authors demonstrate that 11 out of 18 mutations they studied have oncogenic potential, with some of them actionable using clinically available ERBB inhibitors, while giving resistance to EGFR inhibitors.

A very minor comment. At the beginning of page 21, I'd not define PD as the best respone. The Authors can write that all four patients progressed under treatment.

Significance

The work by Ojala et al. is the most detailed study of mutations occurring in ERBB4. Since these are relatively rare, they have not been properly studied up to now. The study is very well done.

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Referee #1

Evidence, reproducibility and clarity

Summary: The authors identify cancer-associated ERBB4 mutations that are selected for functional characterization. Utilizing the BaF3 and MCF10A models, the authors investigate the potential oncogenic role for 11 recurrent ERBB4 mutations. Three mutants (S303F, E452K and L798R) were strongly transforming with the ability to transform both cell models, S303F being unique in its ability to transform both models in the absence of NRG-1. The authors perform modeling to decipher potential mechanisms of action of the ERBB4 S303F, E452K and L798R mutations. The authors assess the ability of HER3 mutations to dimerize with other HER family members and demonstrate that ERBB4 S303F can mediate its activating functions by stabilizing homo- and heterodimers with other ERBB receptors and that the heterodimerization is likely cell/tissue context dependent. The authors demonstrate that transforming ERBB4 mutants are sensitive to pan-ERBB inhibitors and drive resistance to EGFR-targeted therapy in EGFR-mutant NSCLC cells.

Major comments:

1. Patient data analysis is performed in more than 15 months ago in January 2024. This analysis should be updated.
2. The rationale for selecting the mutations to be studied is not entirely clear. There are no references to support studying mutations in Fig 1B red boxes.
3. Cell proliferation should be shown for BaF3 cells for continuity in Figure 2 instead of doubling time. The relative expression of HER3 constructs must be shown for BaF3 and MCF10A cells in Figure 2.
4. Blots in Figure 4 must be quantified.
5. There are major concerns with Supplemental files. It is imperative that the effectiveness of HER3 shRNA be shown in S Fig3. These data are not interpretable without this. Lanes in S Fig 4 are not marked again making data not interpretable.
6. It's unclear why Table 1 is included as this is already published data. This previously published data should be summarized in the text.
7. There is a disconnect why the last two figures focus on a single model of NSCLC whereas the three most transforming mutations are found most commonly in breast, melanoma and GI tract cancers.
8. What are the differences in the recurrent ERBB4 mutant tumors versus ERBB4 wild-type tumors described in Figure 7? Figure 7C, D should be moved to supplemental as this is from previously published data and not strictly relevant to data shown in Fig 7.
9. Limitations should include consideration of endogenous levels of ERBB4 in the model systems used and disparate expression levels of wt ERBB4 versus ERBB4 mutation.

Minor comments:

1. Fig1B lists ERBB3 V104V mutation?
2. List frequency of ERBB4 mutations in the introduction
3. Clarification throughout if cells are serum-starved (how long) if stimulated with NRG-1

Significance

General assessment: This work fills a gap in cancer research understanding if ERBB4 mutations could be targeted. Concerns and comments need to be addressed before definitive conclusions can be made.

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Reply to the reviewers

1. General Statements [optional]

We thank the three reviewers for the time and caution taken to assess our manuscript, and for their constructive feedback that will help improve the study. We herewith provide a revision plan, expecting that the additional experiments and corrections will address the key points raised by the reviewers.

2. Description of the planned revisions

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

• *

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

Summary: The manuscript by Delgado et al. reports the role of the actin remodeling Arp2/3 complex in the biology of Langerhans cells, which are specialized innate immune cells of the epidermis. The study is based on a conditional KO mouse model (CD11cCre;Arpc4fl/fl), in which the deletion of the Arp2/3 subunit ArpC4 is under the control of the myeloid cell specific CD11c promoter.

In this model, the assembly of LC networks in the epidermis of ear and tail skin is preserved when examining animals immediately after birth (up to 1 week). Subsequently however LCs from ArpC4-deleted mice start displaying morphological aberrations (reduced elongation and number of branches at 4 weeks of age). Additionally, a profound decline in LC numbers is reported in the skin of both the ear and tail of young adult mice (8-10 weeks).

To explore the cause of such decline, the authors then opt for the complementary in vitro study of bone-marrow derived DCs, given the lack of a model to study LCs in vitro. They report that ArpC4 deletion is associated with aberrantly shaped nuclei, decreased expression of the nucleoskeleton proteins Lamin A/C and B1, nuclear envelop ruptures and increased DNA damage as shown by γH2Ax staining. Importantly, they provide evidence that the defects evoked by ArpC4 deletion also occur in the LCs in situ (immunofluorescence of the skin in 4-week old mice).

Increased DNA damage is further documented by staining differentiating DCs from ArpC4-deleted mice with the 53BP1 marker. In parallel, nuclear levels of DNA repair kinase ATR and recruitment of RPA70 (which recruits ATR to replicative forks) are reduced in the ArpC4-deleted condition. In vitro treatment of DCs with the topoisomerase II inhibitor etoposide and the Arp2/3 inhibitor CK666 induce comparable DNA damage, as well as multilobulated nuclei and DNA bridges. The authors conclude that the ArpC4-KO phenotype might stem, at least in part, from a defective ability to repair DNA damages occurring during cell division.

The study in enriched by an RNA-seq analysis that points to an increased expression of genes linked to IFN signaling, which the authors hypothetically relate to overt activation of innate nucleic acid sensing pathways.

The study ends by an examination of myeloid cell populations in ArpC4-KO mice beyond LCs. Skin cDC2 and cDC2 subsets display skin emigration defects (like LCs), but not numerical defects in the skin (unlike LCs). Myeloid cell subsets of the colon are also present in normal numbers. In the lungs, interstitial and alveolar macrophages are reduced, but not lung DC subsets. Collectively, these observations suggest that ArpC4 is essential for the maintenance of myeloid cell subsets that rely on cell division to colonize or to self-maintain within their tissue of residency (including LCs).

MAJOR COMMENTS

1. ArpC4 and Arp2/3 expression The authors argue that LCs from Arpc4KO mice should delete the Arpc4 gene in precursors that colonize the skin around birth. It would be important to show it to rule out the possibility that the lack of phenotype (initial seeding, initial proliferative burst) in young animals (first week) could be related to an incomplete deletion of ArpC4 expression. Also important would be to show what is happening to the Arp2/3 complex in LCs from Arpc4KO mice.

__Response: __We thank this reviewer for the careful assessment of our manuscript. Regarding this specific comment, we would like to clarify that we do not expect ArpC4 to be deleted in LC precursors, as CD11c is only expressed once the cells have entered the epidermis. Instead, we expect the deletion to take place after birth around day 2-4 (Chorro et al., 2009). For this reason, we performed a deletion PCR of epidermal cells at postnatal day 7 (P7), a time at which the proliferative burst occurs. This analysis revealed CD11c-Cre-driven recombination in the ArpC4 locus (Fig. S2C). This experiment indicates that ArpC4 deletion does not alter LC proliferation and postnatal network formation.

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Revision plan: We will revise the manuscript text to more clearly explain when ArpC4 will be deleted during development when using the CD11c-Cre transgene, and better emphasize the rationale for the deletion PCR.

In the in vitro studies with DCs, the level of ArpC4 and Arp2/3 deletion at the protein level is also not documented.

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__Response: __We have previously analyzed the expression of ArpC4 in BMDCs in a recent study, confirming its loss in CD11c-Cre;ArpC4fl/fl cells at the protein level: Rivera et al. Immunity 2022; doi: 10.1016/j.immuni.2021.11.008. PMID: 34910930 (Fig. S2D). Therefore, in the current manuscript we only refer to that paper (Results, first paragraph).

The authors explain that surface expression of the CD11c marker, which drives Arpc4 deletion, gradually increased during differentiation of DCs: from 50% to 90% of the cells. Does that mean that loss of ArpC4 expression is only effective in a fraction of the cells examined before day 10 of differentiation (e.g. in the RNA-seq analysis)?

__Response: __The reviewer is correct, there is heterogeneity in CD11c expression, which is inherent of these DC culture model, implying that Arpc4 gene deletion will be partial. However, despite this, we were able to detect significant differences between the transcriptomes of control and CD11c-Cre;ArpC4fl/fl DCs in early phases during differentiation, emphasizing that the phenotype of ArpC4 loss is robust.

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Revision Plan: We will include a notion on this heterogeneity in the revised manuscript text.

Intra-nuclear versus extra-nuclear activities of Arp2/3

The authors favor a model whereby intra-nuclear ArpC4 helps maintaining nuclear integrity during proliferation of DCs (and possibly LCs). However, multiple pools of Arp2/3 have been described and accordingly, multiple mechanisms may account for the observed phenotype: i) cytoplasmic pool to drive the protrusions sustaining the assembly of the LC network and its connectivity with keratinocytes ; ii) peri-nuclear pool to protect the nucleus ; iii) Intra-nuclear pool to facilite DNA repair mechanisms e.g. by stabilizing replicative forks (the scenario favored by the authors).

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__Response: __The referee is correct, and this is actually discussed in our manuscript (page 11, upper paragraph): we cannot exclude that several pools of branched actin are influencing the phenotype we here describe.

Unfortunately, we have previously tested several antibodies against ArpC4, but in our hands, and despite comprehensive optimization, they did not yield specific signals that would enable us to assess changes in subcellular localization in murine cells. Upon this reviewer's comment, we will now reassess the available tools and found an antibody against ArpC2 (Millipore, Anti-p34-Arc/ARPC2, 07-227-I-100UG) that may work based on published data. We have ordered this product to test it for IF staining of ArpC2, hoping to be able to delineate the subcellular localization of ArpC2 in DCs and potentially LCs.

Revision plan: Upon receipt, we will test the ArpC2 antibody (Millipore, #07-227-I-100UG) both in cultured DCs and in epidermal whole mounts, running various optimization protocols regarding fixation, permeabilization and blocking reagents, next to antibody dilution. That way we hope to be able to detect the subcellular localization of Arp2/3 complex components as requested by this reviewer.

It is recommended that the authors try to gather more supportive data to sustain the intra-nuclear role. Documenting ArpC4 presence in the nucleus would help support the claim. It could be combined with treatments aiming at blocking proliferation in order to reinforce the possibility that a main function of ArpC4 is to protect proliferating cells by favoring DNA repair inside the nucleus.

__Response: __We thank this reviewer for this very helpful comment. As outlined in the previous response, we will aim at obtaining subcellular localization data for Arp2/3 complex components, and along with that study a potential intranuclear localization. Beyond that, in comparison to commonly cultured cell types, however, we face two hurdles addressing the nuclear Arp2/3 role in full: 1) Due to poor transduction rates and epigenetic silencing, we cannot sufficiently express exogenous constructs such as ArpC4-NLS in DCs to assess the subcellular localization of Arp2/3 complex components. 2) We have performed preliminary tests to block proliferation in DCs, using the cyclin D kinase 1 inhibitor RO3306 at different concentrations and incubation times during DC differentiation. Unfortunately, most cells were found dead after treatment. Further lowering the inhibitor concentrations (below 3.5uM) will likely not block the cell cycle, rendering this approach unsuited.

Revision plan: We will test the suitability of additional antibodies directed against Arp2/3 complex components to assess their subcellular localization, with the aim to discriminate peripheral cytoplasmic vs. perinuclear vs. intranuclear localization. In addition, we will add a comment in the discussion, further addressing this point. In the case we remain unable to pinpoint that Arp2/3 resides in the nucleus, we will further tone down our current phrasing in the discussion, also emphasizing the possibility that cytoplasmic or perinuclear pools of the complex may indirectly help maintain the integrity of the genome in LCs.

Nuclear envelop ruptures

The nuclear envelop ruptures are not sufficiently documented (how many cells were imaged? quantification?). The authors employ STED microscopy to examine Lamin B1 distribution. The image shown in Figure 4A does not really highlight the nuclear envelop, but rather the entire content. Whether it is representative is questionable. We would expect Lamin B1 staining intensity to be drastically reduced given the quantification shown in Figure 3D. In addition, although the authors have stressed in the previous figure that Arpc4-KO is associated with nucleus shape aberrations, the example shown in Figure 4A is that of a nucleus with a normal ovoid shape.

It is recommended to quantify the ruptures with Lap2b antibodies (or another staining that would better delineate the envelop) in order to avoid the possible bias due to the reduced staining intensity of Lamin B1.

__Response: __NE ruptures were quantified by imaging NLS-GFP-expressing DCs in microchannels to visualize leakage of their nuclear content (Fig. 4B,C). The STED image mentioned by the referee (Fig. 4A,D) was only shown to further illustrate examples of NE ruptures, here using Lamin B as an immunofluorescence marker for the NE. We do agree with the reviewer that it was not chosen optimally to represent the ArpC4-KO phenotype regarding nuclear shape and Lamin B1.

Revision plan: We will provide representative examples of nuclear illustrations of the ArpC4-KO phenotype vs. control cells. In addition, we will perform STED microscopy of Lap2B immunostained DCs as suggested by the referee.

A missing analysis is that of nuclear envelop ruptures as a function of nucleus deformations.

__Response: __As stated in the manuscript (page 5, third paragraph), the morphology of DCs is quite heterogeneous. As mentioned above, nuclear rupture events were quantified by live-imaging of NLS-GFP expressing DCs, enabling the tracing of rupture events. Live imaging is the only robust manner to measure nuclear membrane rupture events as they are transient due to rapid membrane repair (Raab et al. Science 2016). The NLS-GFP label itself, however, is not accurate enough to also quantify nuclear deformations. The latter therefore was quantified after cell fixation, using DAPI and/or immunostaining for NE envelope markers (Figures 3 and S3).

Revision plan: We will quantify nuclear deformations using Lap2B staining of the nuclear envelope as suggested by the referee.

Fig 4B-C: same frequency of Arpc4-KO and WT cells displaying nuclear envelop ruptures in the 4-µm channels; however image show a rupture for the Arpc4-KO and no rupture for the WT cells (this is somehow misleading). Are ruptures similar in Arpc4-KO and WT cells in this condition?

__Response: __We apologize for choosing an image that better reflects our quantification, our mistake.

Revision plan: We will choose an image that better reflects our quantification.

Fig 4D-E: is their a direct link between nuclear envelop ruptures and ƴH2A.X?

__Response: __At present, we can only correlate the findings of increased gH2Ax and elevated events of nuclear envelope ruptures in ArpC4-KO DCs. Rescue experiments are very difficult to impossible in DCs (e.g. restoring Lamin A/C and B levels in the KOs and subsequently assessing the amount of DNA damage). While we are afraid that we cannot address a potential link between NE ruptures and DNA damage by experiments in a manner feasible within this manuscript's revision, we have discussed this interesting aspect based on observations in immortalized cell culture systems (page 10). However, we would like to note that this was indeed shown for different cell types in Nader et al. Cell 2021. This effect results from access of cytosolic nuclease Trex1 to nuclear DNA.

Revision plan: This point will be clarified in our revised manuscript.

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Interesting (but optional) would be to understand what is happening to DNA, histones? Is their evidence for leakage in the cytoplasm?

__Response: __We have not investigated so far. We will attempt to do so.

Revision plan: To address this aspect, we plan to perform immunostainings for double-stranded DNA in the cytoplasm (along with an NE marker). This approach has been used in the field to mark cytoplasmic DNA.

RNA seq analysis

The RNA-seq analysis suffers from a lack of direct connection with the rest of the study. The extracted molecular information is not validated nor further explored. It remains very descriptive. The PCA analysis suggests a « more pronounced transcriptomic heterogeneity in differentiating Arpc4KO DCs ». However it seems difficult to make such a claim from the comparison of 3 mice per group. In addition, such heterogeneity is not seen in the more detailed analysis (Fig 5F). The authors claim that « day 10 control and Arpc4KO DCs showed no to very little differences in gene expression, in contrast to cells at days 7-9 of differentiation ». This is not obvious from the data displayed in the corresponding figure. In addition, it is not expected that cells that may take a divergent differentiation path at days 7-9 may would return to a similar transcriptional activity at day 10.

A point that is not discussed is that before day 10 of DC differentiation, Arpc4 KO is expected to only occur in about 50% of the cell population. This is expected to impact the RNA-seq analysis.

Not all clusters have been exploited (e.g. cluster 3 elevated, cluster 6 partly reduced). I suggest the authors reconsider their analysis and analysis of the RNA-seq analysis (or eventually invest in complementary analysis).

__Response: __Despite a comprehensive analysis of the different transcriptomes of control and ArpC4 mutant cells during DC differentiation, we decided to focus the presentation and discussion of our RNAseq results on the most notable findings. Of these, the elevated innate immune responses in ArpC4-KO DCs (Fig. 5E,H) caught our particular attention, as this seemed highly meaningful in light of DC and LC functions.

Revision plan: As suggested by the referee, in the revised manuscript, we will better connect the RNAseq data to the other cellular and molecular analyses shown, complementing these results by investigating the potential involvement of innate immune responses in the ArpC4-KO phenotype.

What causes the profound numerical drop of LC in the epidermis?

A major open question is what causes the massive drop of LCs. Although differentiating Arpc4KO DCs start accumulating DNA damage upon proliferation, they succeed in progressing through the cell cycle. There is even a slightly elevated expression of cell cycle genes at day 7 of differentiation in the DC model.

Only a trend for increased apoptosis is observed in ear and tail skin. It would be important to provide complementary data documenting increased death (or aberrant emigration?) of LCs in the 4-8 week time window.

__Response: __We agree with the reviewer that this is an important question. We exclude that elevated emigration causes the decline of LCs in ArpC4-KO epidermis, as ArpC4-mutant LCs are significantly reduced (and not increased) in skin-draining lymph nodes (Fig. 7E). To assess whether increased cell death contributed to LC loss, we have tried to identify LCs that are just about to die. As the reviewer noted, we could only observe a trend of apoptosis-positive LCs in mutant epidermis. We assume that this is because of a quick elimination of compromised LCs following DNA damage, with only a short time passing until LCs with impaired genome integrity will be cleared from the system, making it very difficult to detect gH2Ax-positive cells that are positive for markers of cell death.

Revision plan: Despite the abovementioned expected limitations to detect DNA-damage-positive but viable LCs in vivo, for the manuscript revision we will collect 6-week-old mice to analyze LC numbers and apoptosis (cleaved Caspase-3), complementing our data derived from 7-day and 4-week-old mice (Figures S2A,B, S2E,F). Suited mice have been born end of May; we are ready to analyze them at 6-weeks of age, accordingly.

Functional consequences

Although the study reports novel aspects of LC biology, the consequence of ArpC4 deletion for skin barrier function and immunosurveillance are not investigated. It would seem very relevant to test how this model copes with radiation, chemical and/or microorganism challenges.

__Response: __We fully agree with this reviewer that this is a very interesting point. Therefore, next to assessing the steady-state circulation of LCs and DCs, we also addressed the consequence of ArpC4 loss for LC function in chemically challenged skin: we performed skin painting experiments using the contact sensitizer fluorescein isothiocyanate (FITC), diluted in the sensitizing agent dibutyl phthalate (DBP), to detect cutaneous-derived phagocytes within draining lymph nodes. These experiments revealed that migration of Arpc4KO LCs (as well as of Arpc4KO DCs) to skin-draining lymph nodes was impaired (Fig. 7C-E), confirming an in vivo role of ArpC4 for immune cell migration to lymphatic organs following a chemical challenge. Considering the lengthy legal approval procedures for new animal experimentation procedures, additional in vivo challenges -beyond the provided FITC challenge study- would take at least 6 additional months, which would delay excessively the revision of our manuscript.

Revision Plan: We will better explain the FITC painting experiment to highlight its importance.

MINOR COMMENTS:

1- Figure 1D

Gating strategy: twice the same empty plots. The content seems to be missing... Does this need to be shown in the main figure?

__Response: __We apologize for this problem; there might be a problem due to file conversion of PDF reader software. In our PDF versions (including the published bioRxiv preprint) we do see the data points (see below); however, we have earlier experienced incomplete FACS plots during manuscript preparation.

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Revision plan: We will take extra care and double-check the results after converting the figures into PDFs. In addition, we will provide JPG files when submitting the revised manuscript, to prevent such problems.

2- Figure 2

Best would be to keep same scale to compare P1 and P7 (tail skin, figure 2A)

Response and revision plan: We will replace the examples with micrographs of comparable scale (already solved, will be provided with manuscript revision).

Overlay of Ki67 and MHC-II does not allow to easily visualize the double-positive cells (Fig 2C)

Response and revision plan: We will provide single-channel image next to the merged view, and improve the visualization of double-positive cells (already solved, will be provided with manuscript revision)

Quality of Ki67 staining different for Arpc4-KO (less intense, less focused to the nuclei): a technical issue or could that reflect something?

Response and revision plan: We thank the reviewer for spotting this. We have re-assessed all Ki67 micrographs and noted that the originally chosen examples indeed are not fully representative. We have meantime selected more representative examples of Ki67-positive cells in control and mutant tissues, reflecting no difference in the principal nature of Ki67 staining (already taken care of, will be provided with manuscript revision).

Fig 2C: Panels mounted differently for ear and tail skin (different order to present the individual stainings, Dapi for tail skin only).

Response and revision plan: We will harmonize the sequence of panels in figure 2 with submission of the revised manuscript.

3- LC branch analysis (Fig 1 and 2)

While Fig 1 indicates that ear skin LCs form in average twice as few branches as tail skin LCs (3-4 versus 8-9 branches per cell), Fig 2 shows the opposite (10-12 versus 6-7 branches per cell).

Is this due to a very distinct pattern between the 2 considered ages (4 weeks versus 8-10 weeks)? Could the author double-check that there is no methodological bias in their analysis?

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Response: We thank the reviewer for hinting us on this apparent inconsistency. Indeed, our initial analysis suffered from a bias in detecting LC dendrites, as the tissue cellularity and overall morphology significantly differs between 4-week-old and adult animals: In adult animals, the immunostainings show a higher baseline background signal for the skin epithelium compared to P28. We had noted this beforehand and had adjusted the imaging pipeline accordingly, with a more stringent thresholding to eliminate background signals in the case of adult tissues. While we were able to detect the described ArpC4 phenotype, this strategy resulted in a reduced ability to detect dendrites (both in control and mutant tissues), explaining the seemingly reduced number of dendrites in adult vs. 4-week-old tissues.

Revision plan: We have double-checked both the micrographs and the corresponding quantifications and did not identify errors. Instead, our assumption -that a too high stringency for background reduction in adults caused the discrepancy- turned out correct. At present, we are re-doing the detailled analyses of LC morphology at 4-week and adult stages by confocal microscopy using a 63x objective rather than a 40x objective as done previously. First results confirm that with this approach the number of LC dendrites across these ages are largely comparable, while the phenotypes of ArpC4 loss are retained. We will provide a completely new analysis with revision of the manuscript.

4- Fig 3 E-G

How many animals were examined (n=5)? Reproducible accros animals? Why was it done with 4-week animals (phenotype not complete? Event occurring before loss in numbers...)

Response and revision plan: As mentioned in the figure legend for Fig. 3F we have analysed N = 4 control and N= 5 KO mice (for clarity, we will add this information to Figure 3E and G in the revised document). We chose the 4-week time-point as this was the stage when the loss of LCs first became apparent (even though non-significant at this age). We aimed to learn whether changes in nuclear morphology and nuclear envelope markers represented early molecular and cellular events following ArpC4 loss. Compared to later stages, this strategy poses a reduced risk to detect indirect effects of ArpC4 loss. We will clarify this in the revised manuscript text.

Staining Lamin A/C globally more intense in the Arpc4-KO epidermis (also seems to apply to the masks corresponding to the LCs). Surprising to see that the quantification indicates a major drop of Lamin A/C intensity in the LCs.

Response and revision plan: We again thank the reviewer for this careful assessment. The originally chosen micrographs are indeed not fully representative. As with many tissue stainings, there is inter-sample variability. We have now revisited the micrographs and did not find a significant global reduction of Lamin A/C in the entire epidermis (including keratinocytes/KCs). The drop of Lamin A/C intensity is restricted to ArpC4 LCs -and not KCs- and in line with the reduced Lamin A/C expression data in DCs (Fig. 3C,D). We have selected more representative examples, which will be provided with the revised manuscript.

Legend Fig 4D replace confocal microscopy by STED microscopy

Revision plan: We will replace "confocal microscopy" by "STED microscopy" accordingly.

6- Figure 4F

Intensity/background of γH2Ax staining very distinct between the 2 micrographs shown for WT and Arpc4-KO epidermis.

Response and revision plan: We have revisited the micrographs and now selected more representative examples, which will be provided in the revised manuscript.

7- Figure 7C, F, H

Gating strategies: would be better to harmonize the style of the plots (dot plots and 2 types of contour plots have been used...)

Response and revision plan: We agree and will provide a harmonized plot illustration in the revised manuscript.

8- Figure 7H

Legend of lower gating strategy seems to be wrong (KO and not WT).

Response and revision plan: We thank the reviewer for pointing out this mistake. A corrected figure display will be provided with revision.

Reviewer #1 (Significance (Required)):

Strengths: the general quality of the manuscript is high. It is very clearly written and it contains a very detailed method section that would allow reproducing the reported experiments. This work entails a clear novelty in that it represents the first investigation of the role of ArpC4 in LCs. It opens an interesting perspective about specific mechanisms sustaining the maintenance of myeloid cell subsets in peripheral tissues. This work is therefore expected to be of interest for a large audience of cellular immunologists and beyond. Challenging skin function with an external trigger would lift the relevance for a even wider audience (see main point 6).

__Response: __see point 6.

Limitations: in its current version the manuscript suffers from a lack of solidity around a few analysis (see main points on ArpC4 and Arp2/3 protein expression, nuclear envelop rupture analysis,...). It also tends to formulate a narrative centered on the ArpC4 intra-nuclear function that is not definitely proven.

The field of expertise of this reviewer is: cellular immunology and actin remodeling.

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

SUMMARY This is a study in experimental mice employing both in vitro and, importantly, in vivo approaches. EPIDERMAL LANGERHANS CELLS serve as a paradigm for the maintenance of homeostasis of myeloid cells in a tissue, epidermis in this case. In addition to well known functions of the ACTIN NETWORK in cell migration, chemotaxis, cell adherence and phagocytosis the authors reveal a critical function of actin networks in the survival of cells in their home tissue.

Actin-related proteins (Arp), specifically here the Arp2/3 complex, are necessary to form the filamentous actin networks. The authors use conditional knock-out mice where Arpc4 (an essential component of the Arp2/3 complex) is deleted under the control of CD11c, the most prominent dendritic cell marker which is also expressed on Langerhans cells. In normal mice, epidermal Langerhans cells reside in the epidermis virtually life-long. They initially settle the epidermis around and few days after birth an establish a dense network by a burst of proliferation and then they "linger on" by low level maintenance proliferation. In the epidermis of Arpc4 knock-out mice Langerhans cells also start off with this proliferative burst but, strikingly, they do not stay but are massively reduced by the age of 8-12 weeks.

The analyses of this decline revealed that

-- the shape (number of nuclear lobes) and integrity of cell nuclei was compromised; they were fragile and ruptured to some degree when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- DNA damage, as detected by staining for gamma-H2Ax or 53BP1 accumulated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- recruitment of DNA repair molecules was inhibited when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- gene signatures of interferon signaling and response were increased when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- in vivo migration of dendritic cells and Langerhans cells from the skin to the draining lymph nodes in an inflammatory setting (FITC painting of the skin) was impaired when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

-- the persistence of the typical dense network of Langerhans cells in the epidermis, created by proliferation shortly after birth, is abrogated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing. Importantly, this was not the case for myeloid cell populations that settle a tissue without needing that initial burst of proliferation. For instance, numbers of colonic macrophages were not affected when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing.

Thus, the authors conclude that the Arp2/3 complex is essential by its formation of actin networks to maintain the integrity of nuclei and ensure DNA repair thereby ascertaining the maintenance proliferation of Langerhans cells and, as the consequence, the persistence of the dense epidermal netowrk of Langerhans cells.

Up-to-date methodology from the fields of cell biology and cellular immunology (cell isolation from tissues, immunofluorescence, multiparameter flow cytometry, FISH, "good old" - but important - transmission electronmicroscopy, etc.) was used at high quality (e.g., immunofluorescence pictures!). Quantitative and qualitative analytical methods were timely and appropriate (e.g., Voronoi diagrams, cell shape profiling tools, Cre-lox gene-deletion technology, etc.). Importantly, the authors used a clever method, that they had developed several years ago, namely the analysis of dendritic cell migration in microchannels of defined widths. Molecular biology methods such as RNAseq were also employed and analysed by appropriate bioinformatic tools.

MAJOR COMMENTS:

• ARE THE KEY CONCLUSIONS CONVINCING? Yes, they are.

• SHOULD THE AUTHORS QUALIFY SOME OF THEIR CLAIMS AS PRELIMINARY OR SPECULATIVE, OR REMOVE THEM ALTOGETHER? No, I think it is ok as it stands. The authors are wording their claims and conclusions not apodictically but cautiously, as it should be. They point out explicitely which lines of investigations they did not follow up here.

• 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. I think that the here presented experimental evidence suffices to support the conclusions drawn. No additional experiments are necessary.

• 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. Not applicable.

• ARE THE DATA AND THE METHODS PRESENTED IN SUCH A WAY THAT THEY CAN BE REPRODUCED? Yes, they are.

• ARE THE EXPERIMENTS ADEQUATELY REPLICATED AND STATISTICAL ANALYSIS ADEQUATE? Yes.

__Response: __We thank the reviewer very much for assessing our work, for providing constructive suggestions, and for acknowledging the strength of the study.

MINOR COMMENTS:

• SPECIFIC EXPERIMENTAL ISSUES THAT ARE EASILY ADDRESSABLE. None

• ARE PRIOR STUDIES REFERENCED APPROPRIATELY? Essentially yes. Regarding the reduction / loss of the adult epidermal Langerhans cell network, it may be of some interest to also refer to / discuss to another one of the few examples of this phenomenon. There, the initial burst of proliferation is followed by reduced proliferation and increased apoptosis when a critical member of the mTOR signaling cascade is conditionally knocked out (Blood 123:217, 2014).

__Response and revision plan: __As suggested, we will include into the revised manuscript further examples with related phenotypes regarding the progressive decline of LCs.

• ARE THE TEXT AND FIGURES CLEAR AND ACCURATE? Yes they are. Figures are well arranged for easy comprehension.

• DO YOU HAVE SUGGESTIONS THAT WOULD HELP THE AUTHORS IMPROVE THE PRESENTATION OF THEIR DATA AND CONCLUSIONS?

1. Materials & Methods. The authors write, regarding flow cytometry of epidermal cells: "Briefly, 1cm2 of back skin from 8-14 weeks old female wild-type and knockout littermates was dissociated in 0.25 mg/mL Liberase (Sigma, cat. #5401020001) and 0.5 mg/mL DNase (Sigma, cat.#10104159001) in 1 mL of RPMI (Sigma) and mechanically disaggregated in Eppendorf tubes, FOLLOWED BY INCUBATED for 2 h at 37 {degree sign}C." Followed by what?

__Response and revision plan: __We apologize for this mistake. The text should read: "... followed by blocking and antibody labeling of cells in single cell suspension.". We will provide the correct text in the revised manuscript.

Materials & Methods. BMDC electronmicroscopy. What is "IF". Please specify.

__Response and revision plan: __We also regret this mistake in the method text. It should read: "... For electron microscopy analysis, after PDMS removal, cells were fixed using 2.5% glutaraldehyde ...". We will correct this in the revised manuscript.

RESULTS in gene expression analyses. The authors observe some increase in apoptosis (as detected by cleaved-Caspase-3 staining). Is this observation in immunofluorescence also evident in the RNAseq data (where the IFN changes were seen), i.e., in Figure 5.

__Response and revision plan: __We will check our RNAseq data regarding any changes in apoptosis-related genes and, if so, include these in the revised manuscript.

Figure 7 F and G. Perhaps the authors may want to swap upper and lower panels in F or G, so that macrophage FACS plots and bar graphs are in the same row - ob, obiously, DC plots and bars likewise.

__Response and revision plan: __We agree and will harmonize the panel sequence in the revised manuscript.

Figure 7H. "Gating strategy in ArpC4WT Lung (previously gated in Live CD45+ cells)" - The lower row is knock-out, not WT. This is indicated correctly in the legand, but in the figure both rows are labeled as WT.

__Response and revision plan: __Indeed, the legend information is correct, but the corresponding figure panel is incorrect. We will provide a corrected version with revision.

The reference by Park et al. 2021 is missing in the list.

__Response and revision plan: __We will add the reference to the revised bibliography.

Figure 1D. Sure, the bar graphs are meant to say "CD11c"? The FACS plots show "CD11b".

__Response and revision plan: __We will check the panels and correct where necessary.

As to cDC1. In Figure 1D the FACS plot shows an absence of CD103+ cDC1 cells. In contrast, In Figure 7A-left side panel, there is not difference in cDC1 cells between WT and KO mice. Is therefore the flow cytometry plot in Figure 1D not representative regarding cDC1 cells? Correct?

__Response and revision plan: __The reviewer is correct about this apparent discrepancy. We have not observed differences in the control vs. Aprc4-KO cDC1 population, hence Figure 7 represents our findings. For figure 1, we have by mistake chosen a non-representative plot, with the aim of illustrating the gating strategy. We apologize for this mistake and will provide a corrected an representative FACS plot figure in the revised manuscript.

Reviewer #2 (Significance (Required)):

• DESCRIBE THE NATURE AND SIGNIFICANCE OF THE ADVANCE (E.G. CONCEPTUAL, TECHNICAL, CLINICAL) FOR THE FIELD. This is a conceptual advance. It adds a big step to our understanding of how immune cells in tissues (which all come from the bone marrow or are seeded before birth from embryonal hematopoietic organs such as yolk sac and fetal liver) can remain resident in these tissues. For cell types such as Langerhans cells, which establish their final population density within their tissues of residence, the presented finding convincingly buttress the role of proliferation and thereby the role for the actin-related protein complex 2/3 (Arp2/3).

• PLACE THE WORK IN THE CONTEXT OF THE EXISTING LITERATURE (PROVIDE REFERENCES, WHERE APPROPRIATE). While we know much about actin-related proteins (Arp), as correctly cited by the authors, this knowledge is derived mostly from in vitro studies. The submitted study translates the findings to an in vivo setting for the first time.

• STATE WHAT AUDIENCE MIGHT BE INTERESTED IN AND INFLUENCED BY THE REPORTED FINDINGS. Skin immunologists foremost, but these findings are of interest to the entire community of immunologists, but also cell biologists.

• DEFINE YOUR FIELD OF EXPERTISE. My expertise is in skin immunology, in particular skin dendritic cells including Langerhans cells.

We acknowledge the referee for their positive assessment of our manuscript.

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

Summary:

The manuscript identifies a role of the Arp2/3 complex, the major regulator of actin branching in cells, for controlling the homeostasis of murine Langerhans cells (LCs), a specialized subset of dendritic cells in the skin epidermis. The findings of the study are based on the analysis of CD11c-Cre Arpc4-flox mice, a conditional knockout mouse model, which interferes with Arp2/3 function in Langerhans cells and other CD11c-expressing myeloid cells, e.g. dendritic cell or macrophage subsets. By using immunofluorescence and flow cytometry analysis of epidermis and skin tissues, the authors provide a detailed analysis of LC numbers at different developmental stages (postnatal day 1, 7, 28, and adult mice) and demonstrate that Arpc4-deficiency does not interfere with the establishment of LC networks until postnatal day 28. However, LCs in ear and tail skin are substantially reduced in Arpc4-deficient mice at 8-12 weeks of age. In parallel to their in vivo model, the authors analyze cultures of bone marrow-derived dendritic cells (BMDCs) from control and CD11c-Cre Arpc4-flox mice. Arpc4-deficiency in BMDCs, which develop over 8-10 days in culture, results in nuclear shape and lamina abnormalities, as well as signs of increased DNA damage. Aspects of this phenotype are also detected in Langerhans cells in epidermal preparations. Transcriptomic analysis of BMDCs highlights a gene signature of increased expression of the interferon response pathway and alterations in cell cycle regulation. Arpc4-deficient BMDCs show increased expression of DNA damage markers and reduced expression of certain DNA repair factors. Based on these correlative findings from the BMDC model, the authors conclude that the decline in LC numbers might develop from the accumulation of DNA damage over time, which the authors phrease "pre-mature aging of Langerhans cells". Lastly, the authors show a heterogenous picture how Arp2/3 depletion affects distinct DC populations in CD11c-Cre Arpc4-flox mice. While some tissue-resident DC subsets appear normal in numbers, others are declined in numbers in the tissue. This may be related to their proliferation potential in tissues.

Major comments:

• Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

1) The authors claim that Arpc4 deficiency selectively compromises myeloid cell populations that rely on proliferation for tissue colonization (Figure 7). The presented data might give hints for such a general hypothesis, but solid experimental proof to prove this is lacking. When comparing myeloid cell subsets from foru different irgans, the authors refer to published data that some dendritic cell subsets are more proliferative in tissues than others and that CD11cCre Arpc4-flox mice appear to have reduced cell numbers in these populations. However, the presented data are purely correlative and no functional connection to cell proliferation has been made to the phenotypes. While some dendritic cell subsets (Langerhans cells, alveolar DCs) show reduced cell numbers in CD11cCre Arpc4-flox mice, other myeloid cell cells subsets are unaffected (e.g. dermal cDC1 and 2, colon macrophages).There could be plenty of other reasons that might underly the observed discrepancies between these cell subsets, e.g. Arp2/3 knockout efficiency and myeloid cell turnover in the tissue are just two examples, which have not been taken into consideration. Direct measurement of cell proliferation, e.g. BrdU labeling, and the observed phenotype would be missing to make such claims. The data could either be removed. Experimentally addressing these points could take 3-6 months.

Response and planned revisions: We thank the referee for bringing this point. We agree that these results give hints that support our conclusion but that do not address this question directly. However, we would like to insist on the fact that our conclusion is based on studies from others showing that alveolar macrophages self-maintain themselves through proliferation (Bain et al. Mucosal Immunology 2022). In contrast, it has been reported that most colonic macrophages are derived from monocytes that are being recruited to the gut through life (Bain et al. Mucosal Immunity 2023)

We propose to better explain and discuss these points in our revised manuscripts. In addition, we will stress that we do not exclude that different intracellular Arpc4-dependent processes might contribute to the phenotypes observed (beyond maintenance of DNA integrity). These revisions will help mitigate our conclusions and leave open the potential implication of alternative mechanisms that will be discussed as suggested by the referee.

2) The authors claim that DC subsets (e.g. dermal cDCs), which develop from pre-DCs, are not affected by Arp2/3 depletion (Figure 7, although the FACS plot in Fig. 1D would suggest a different picture for cDC1). This is surprising in light of the data with bone marrow-derived DCs (BMDCs), the major in vitro model of this study, which develop from CDPs that again develop from pre-DCs. BMDCs did show aberrant nuclei and signs of DNA damage. How would the authors then explain the discrepancies of the BMDC model with DC subsets, where the authors feel that the pre-DC origin explains the phenotypic difference? This is a general concern of the data interpretation and conclusions.

__Response: __We thank the referee to bring this point that indeed requires clarification. Two non-exclusive hypotheses could explain this apparent discrepancy:

• The ontogeny of bone-marrow-derived DCs: Depending on the protocol used, there might be variations in the precursors DCs develop from. We use one of the first protocols, which was pioneered by Paola Ricciardi-Castagnoli lab (Winzler et al. J.Exp.Med. 1997). It relies on a supernatant from J558 cells transfected with GMCSF, which contains additional cytokines and mainly generate DC2-like DCs. Langerhans cells are closer to DC2s, which resemble more macrophages than DC1s. We thus chose this protocol rather than the protocols that use Flt3-L, which produce both DC1s and DC2s developed from common dendritic-cell precursors (CDPs). It is thus possible that our BM-derived DCs develop from other precursor cells that are possibly closer to monocyte precursors.
• As shown in Figure 5C, kinetics of acquisition of CD11c expression, and thus deletion of the Arpc4 gene, might be distinct in vivo and in vitro. In vivo, as stated in our manuscript, DCs acquire CD11c as preDCs and undergo few rounds of divisions after. In vitro, as shown by our cycling experiments, BM-derived DCs continuously cycle, so they will keep dividing after having acquire CD11c (around day 7) and deleting the Arpc4 gene. __Revision plan: __We propose to mention these hypotheses in the discussion of our manuscript to explain the apparent contradiction raised by the referee.

3) In line with point 2, the authors never show that BMDCs show reduced proliferation, reduced cell numbers or increased cell death in Arpc4-deficient cell cultures, as a consequence of the detected DNA damage and impaired DNA repair. In fact, Figure 5C even shows that cell growth rates between control and KO are equal. This is a major mismatch in the current study. Since the authors use the BMDC model to explain the declining cell numbers in Langerhans cells (which derive from fetal liver cells), this phenotype is not mirrored by the BMDC culture and it remains open whether the observed changes in nuclear DNA damage and repair are indeed directly linked to the observed phenotype of declining cell numbers in the tissue. These aspects require argumentation why cell growth is unchanged in KO cells. Additional experiments addressing these points with sufficient biological replicates (cultures from different mice) could take 2-3 months, including preparation time.

__Response____: __We thank the referee for bringing this point, which was probably not properly discussed in the first version of our manuscript. Indeed, Arpc4KO BM-derived DCs do not show the premature cell death phenotype observed in LCs in vivo, as stated by the referee. There are at least two putative non-exclusive explanations for this. First, unlike LCs, which are long-lived cells, BM-derived DCs can be kept in culture for only 10-12 days. As DNA damage-induced cell death takes time (LCs only start to die about 3-4 weeks after network establishment), the lifespan of BM-DCs could simply not be long enough to observe this phenotype. Second, in the epidermis, LCs are physically constrained and continuously exposed to diverse signals that might increase their sensitivity to DNA damage and thereby induction of subsequent cell death.

__Revision Plan: __We will clarify this point in our revised manuscript by providing putative explanations for the death phenotype of Arpc4-deficient LCs not being observed in BM-derived DCs. We will further explain that this does not invalidate this cellular model as it was used to raise hypotheses on the putative role played by Arpc4 in myeloid cells, i.e. maintenance of DNA integrity, which was then confirmed in vivo (Arpc4KO LCs do indeed display DNA damage in the epidermis). Without this "imperfect cellular model", we would have probably not been able to uncover this novel function of Arp2/3 in immune cells.

4) The authors refer to a "pre-mature aging" phenotype of Arpc4-deficient BMDCs and LCs, based on reductions in Lamin B, Lamin A and increases in gH2AX and 53BP1. I find this term and overstatement of the current data and suggest that other markers for cell senescence, such as p53, Rb, p21 and b-Galactosidase are then also used to make such strong claim on "aging" and cell senescence. Experimentally addressing this point with sufficient biological replicates could take 2-3 months, including preparation time.

__Revision Plan: __We will assess the expression of these genes and senescence signatures in our RNAseq analysis as well as in Arpc4WT and Arpc4KO-derived DCs, as suggested by the referee.

5) The study does not provide a mechanism how the Arp2/3 complex would mediate the observed effects on DNA damage and repairs has not been addressed in the cell model, and only potential scenarios from other non-myeloid cell lines are discussed. It remains unclear whether the observed phenotypes in Arpc4-depleted myleoid cells relate to the direct nuclear function of Arp2/3 or the cytosolic function of Arp2/3, including its roles in cytoskeletal regulation that may have secondary effects on the nuclear alterations. This is a general concern of the presented data, data on mechanism might require more than 6 months.

__Revision Plan: __The referee is correct: Our manuscript shows that Arp2/3 deficiency in specific myeloid cells impacts on their survival in vivo and proposes that this could result at least in part from impaired maintenance of DNA integrity in these cells. We do not know whether this also applies to non-myeloid cells, which, although very interesting, is beyond the scope of the present study. In addition, we do not have any experimental tool to distinguish whether the DNA damage phenotype of Arpc4KO cells involves the nuclear or cortical pool of F-actin, this is why we have left this question open in the discussion of our manuscript.

6) OPTIONAL: The authors make a strong case arguing that the increased interferon expression signature (based on the transcriptomics data) reflects the nuclear ruptures in Arpc4-deficient cells and adds to the observed phenotype. If this is so, what happens then in STING knockout cells in the presence of CK666 inhibitor?

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__Revision Plan____: __The referee is correct in that we do not show this point experimentally and should therefore temper this conclusion.

• Are the data and the methods presented in such a way that they can be reproduced?

1) The analyses include quite a number of intensity calculations of immunofluorescence signals (Fig. 3D, E; Fig. 4E, Fig. 5B and 6B)? The background stainings are often variable or very high. In some cases it is even unclear whether stainings are really detecting protein and go beyond background staining (Fig. 6A, Fig. 5F). How were immunofluorescence data acquired and dealt with different background staining intensities?

__Revision Plan: __We will carefully describe the microscopes used for image acquisition as well as the downstream analyses for each experiment, which indeed vary depending on the signals observed with distinct antibodies or construct.

2) It remained unclear to me on which basis the nuclear deformations in Fig. 3G, H were calculated?

__Revision Plan: __We will carefully describe the methods used to quantify nuclear deformations.

3) The detailed phenotype of control mice is a bit unclear. It appears as if these were Cre-negative animals. Did the authors have some proof-of-principle experiments showing that CD11cCre Arpc4 +/+ animals have comparable phenotypes to Cre-negative animals?

• Are the experiments adequately replicated and statistical analysis adequate?

__Revision Plan: __We have never observed any decline in LC numbers in other mouse lines/genotypes (for example in cPLA2flox/flox;CD11c-Cre mice shown in the manuscript, Fig. S6B), excluding a putative role for the Cre in LC death.

For most experiments, the number of biological replicates (mice, or BMDC cultures from different mice) and individual values (n, cells) are indicated. Statistical analysis appears adequate.

Minor comments:

• Prior published studies on Arp2/3 function in immune cells are referenced accordingly. A number of additional pre-print manuscripts on this topic have not been cited and could be considered referencing.

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__Revision Plan: __We will fix this point and cite additional, relevant preprints.

• The text is very clearly and very well written. Figures are clear and accurate for most cases. There are some open questions:

• Fig. 1B: The number of dots betwenn graph and legend do not match. The dots are not n=12 for both genotypes. Additionally: What do the symbols in the circles in the graph stand for? This is also in another later figure unclear.

• Fig. 2C: The current IF presentation (overlay MHCII with Ki67) is not very helpful. An additional image that shows only the Ki67 signal in the MHCII mask would be very helpful.

• Fig. 4B: BMDCs of which culture day were used for these experiments?

• Fig. 4A and D shows the same representative cells for two biological messages, which is only moderately convincing regarding a "general" phenotype.

• Fig. 5, B: Scale bars are missing.

__Revision Plan: __We will fix all these points.

Reviewer #3 (Significance (Required)):

Strengths and Advance:

The study provides strong data and a very detailed analysis of how the Arp2/3 complex regulates stages of Langerhans cell development and homeostasis. The role of the Arp2/3 complex as regulator of actin branching, which is involved in many cellular functions, has previously not been reported for this cell type. Previous research in immune cells have already studied the Arp2/3 complex, but studies were focussed on its role in migration and the majority of published phenotypes related to cell migration. While there are already a number of in vitro studies showing that the Arp2/3 complex can regulate aspects of cell cycle control or cell death in non-immune cells, most of these studies were performed with immortalized, non-immune cell lines, which can be more easily manipulated to dissect mechanistic aspects of the cellular phenotype, but are limited in their physiological interpretation. Hence, it is a major strength of this study to investigate the effects of Arp2/3 in a primary immune cell type, directly in the native and physiological environment. This is important because in vitro data from other cell types cannot be easily extrapolated to any other cell type and it is critical for our understanding to collect physiological data from tissues, where the biology really happens. The finding that the Arp2/3 complex regulates the tissue-residency of Langerhans cell through processes that are unrelated to migration are partially unexpected, shifting the view of this protein complex's physiological role to other cell biological processes, e.g. regulation of cell proliferation.

Limitations: The limitations of the study are detailed in the five major points listed above. The study accumulates many experiments that characterize the phenotype of Arpc4-depleted cells, showing signs of DNA damage in Langerhans cells and cultures of BMDCs. How the Arp2/3 complex would mechanistically mediate the observed effects on DNA damage and repairs have not been addressed. It also remains open whether this is due to the effects of the Arp2/3 complex in the nucleus or the cytosol, which would be biologically extremely important to understand. Above that, there are some discrepancies regarding the phenotype of the BMDC model, which does neither entirely match the Langerhans cell phenotype in the tissue (reduced proliferation, LC derive from different progenitors), nor other endogenous DC populations, which should also derive from similar progenitors.

Audience and reviewer background:

In its current form, the manuscript will already be of interest for several research fields: Langerhans cell and dendritic cell homeostasis, immune cell trafficking, actin and cytoskeleton regulation in immune cells, physiological role of actin-regulating proteins. My own field of expertise is immune cell trafficking in mouse models, leukocyte migration and cytoskeletal regulation. I cannot judge the analysis and clustering of the bulk RNA sequencing data.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The manuscript identifies a role of the Arp2/3 complex, the major regulator of actin branching in cells, for controlling the homeostasis of murine Langerhans cells (LCs), a specialized subset of dendritic cells in the skin epidermis. The findings of the study are based on the analysis of CD11c-Cre Arpc4-flox mice, a conditional knockout mouse model, which interferes with Arp2/3 function in Langerhans cells and other CD11c-expressing myeloid cells, e.g. dendritic cell or macrophage subsets. By using immunofluorescence and flow cytometry analysis of epidermis and skin tissues, the authors provide a detailed analysis of LC numbers at different developmental stages (postnatal day 1, 7, 28, and adult mice) and demonstrate that Arpc4-deficiency does not interfere with the establishment of LC networks until postnatal day 28. However, LCs in ear and tail skin are substantially reduced in Arpc4-deficient mice at 8-12 weeks of age. In parallel to their in vivo model, the authors analyze cultures of bone marrow-derived dendritic cells (BMDCs) from control and CD11c-Cre Arpc4-flox mice. Arpc4-deficiency in BMDCs, which develop over 8-10 days in culture, results in nuclear shape and lamina abnormalities, as well as signs of increased DNA damage. Aspects of this phenotype are also detected in Langerhans cells in epidermal preparations. Transcriptomic analysis of BMDCs highlights a gene signature of increased expression of the interferon response pathway and alterations in cell cycle regulation. Arpc4-deficient BMDCs show increased expression of DNA damage markers and reduced expression of certain DNA repair factors. Based on these correlative findings from the BMDC model, the authors conclude that the decline in LC numbers might develop from the accumulation of DNA damage over time, which the authors phrease "pre-mature aging of Langerhans cells". Lastly, the authors show a heterogenous picture how Arp2/3 depletion affects distinct DC populations in CD11c-Cre Arpc4-flox mice. While some tissue-resident DC subsets appear normal in numbers, others are declined in numbers in the tissue. This may be related to their proliferation potential in tissues.

Major comments:

• Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

1) The authors claim that Arpc4 deficiency selectively compromises myeloid cell populations that rely on proliferation for tissue colonization (Figure 7). The presented data might give hints for such a general hypothesis, but solid experimental proof to prove this is lacking. When comparing myeloid cell subsets from foru different irgans, the authors refer to published data that some dendritic cell subsets are more proliferative in tissues than others and that CD11cCre Arpc4-flox mice appear to have reduced cell numbers in these populations. However, the presented data are purely correlative and no functional connection to cell proliferation has been made to the phenotypes. While some dendritic cell subsets (Langerhans cells, alveolar DCs) show reduced cell numbers in CD11cCre Arpc4-flox mice, other myeloid cell cells subsets are unaffected (e.g. dermal cDC1 and 2, colon macrophages).There could be plenty of other reasons that might underly the observed discrepancies between these cell subsets, e.g. Arp2/3 knockout efficiency and myeloid cell turnover in the tissue are just two examples, which have not been taken into consideration. Direct measurement of cell proliferation, e.g. BrdU labeling, and the observed phenotype would be missing to make such claims. The data could either be removed. Experimentally addressing these points could take 3-6 months.

2) The authors claim that DC subsets (e.g. dermal cDCs), which develop from pre-DCs, are not affected by Arp2/3 depletion (Figure 7, although the FACS plot in Fig. 1D would suggest a different picture for cDC1). This is surprising in light of the data with bone marrow-derived DCs (BMDCs), the major in vitro model of this study, which develop from CDPs that again develop from pre-DCs. BMDCs did show aberrant nuclei and signs of DNA damage. How would the authors then explain the discrepancies of the BMDC model with DC subsets, where the authors feel that the pre-DC origin explains the phenotypic difference? This is a general concern of the data interpretation and conclusions.

3) In line with point 2, the authors never show that BMDCs show reduced proliferation, reduced cell numbers or increased cell death in Arpc4-deficient cell cultures, as a consequence of the detected DNA damage and impaired DNA repair. In fact, Figure 5C even shows that cell growth rates between control and KO are equal. This is a major mismatch in the current study. Since the authors use the BMDC model to explain the declining cell numbers in Langerhans cells (which derive from fetal liver cells), this phenotype is not mirrored by the BMDC culture and it remains open whether the observed changes in nuclear DNA damage and repair are indeed directly linked to the observed phenotype of declining cell numbers in the tissue. These aspects require argumentation why cell growth is unchanged in KO cells. Additional experiments addressing these points with sufficient biological replicates (cultures from different mice) could take 2-3 months, including preparation time.

4) The authors refer to a "pre-mature aging" phenotype of Arpc4-deficient BMDCs and LCs, based on reductions in Lamin B, Lamin A and increases in gH2AX and 53BP1. I find this term and overstatement of the current data and suggest that other markers for cell senescence, such as p53, Rb, p21 and b-Galactosidase are then also used to make such strong claim on "aging" and cell senescence. Experimentally addressing this point with sufficient biological replicates could take 2-3 months, including preparation time.

5) The study does not provide a mechanism how the Arp2/3 complex would mediate the observed effects on DNA damage and repairs has not been addressed in the cell model, and only potential scenarios from other non-myeloid cell lines are discussed. It remains unclear whether the observed phenotypes in Arpc4-depleted myleoid cells relate to the direct nuclear function of Arp2/3 or the cytosolic function of Arp2/3, including its roles in cytoskeletal regulation that may have secondary effects on the nuclear alterations. This is a general concern of the presented data, data on mechanism might require more than 6 months.

6) OPTIONAL: The authors make a strong case arguing that the increased interferon expression signature (based on the transcriptomics data) reflects the nuclear ruptures in Arpc4-deficient cells and adds to the observed phenotype. If this is so, what happens then in STING knockout cells in the presence of CK666 inhibitor?

• Are the data and the methods presented in such a way that they can be reproduced?

1) The analyses include quite a number of intensity calculations of immunofluorescence signals (Fig. 3D, E; Fig. 4E, Fig. 5B and 6B)? The background stainings are often variable or very high. In some cases it is even unclear whether stainings are really detecting protein and go beyond background staining (Fig. 6A, Fig. 5F). How were immunofluorescence data acquired and dealt with different background staining intensities?

2) It remained unclear to me on which basis the nuclear deformations in Fig. 3G, H were calculated?

3) The detailed phenotype of control mice is a bit unclear. It appears as if these were Cre-negative animals. Did the authors have some proof-of-principle experiments showing that CD11cCre Arpc4 +/+ animals have comparable phenotypes to Cre-negative animals?

• Are the experiments adequately replicated and statistical analysis adequate?

For most experiments, the number of biological replicates (mice, or BMDC cultures from different mice) and individual values (n, cells) are indicated. Statistical analysis appears adequate.

Minor comments:

• Prior published studies on Arp2/3 function in immune cells are referenced accordingly. A number of additional pre-print manuscripts on this topic have not been cited and could be considered referencing.

• The text is very clearly and very well written. Figures are clear and accurate for most cases. There are some open questions:

1) Fig. 1B: The number of dots betwenn graph and legend do not match. The dots are not n=12 for both genotypes. Additionally: What do the symbols in the circles in the graph stand for? This is also in another later figure unclear.

2) Fig. 2C: The current IF presentation (overlay MHCII with Ki67) is not very helpful. An additional image that shows only the Ki67 signal in the MHCII mask would be very helpful.

3) Fig. 4B: BMDCs of which culture day were used for these experiments?

4) Fig. 4A and D shows the same representative cells for two biological messages, which is only moderately convincing regarding a "general" phenotype.

5) Fig. 5, B: Scale bars are missing.

Significance

Strengths and Advance:

The study provides strong data and a very detailed analysis of how the Arp2/3 complex regulates stages of Langerhans cell development and homeostasis. The role of the Arp2/3 complex as regulator of actin branching, which is involved in many cellular functions, has previously not been reported for this cell type. Previous research in immune cells have already studied the Arp2/3 complex, but studies were focussed on its role in migration and the majority of published phenotypes related to cell migration. While there are already a number of in vitro studies showing that the Arp2/3 complex can regulate aspects of cell cycle control or cell death in non-immune cells, most of these studies were performed with immortalized, non-immune cell lines, which can be more easily manipulated to dissect mechanistic aspects of the cellular phenotype, but are limited in their physiological interpretation. Hence, it is a major strength of this study to investigate the effects of Arp2/3 in a primary immune cell type, directly in the native and physiological environment. This is important because in vitro data from other cell types cannot be easily extrapolated to any other cell type and it is critical for our understanding to collect physiological data from tissues, where the biology really happens. The finding that the Arp2/3 complex regulates the tissue-residency of Langerhans cell through processes that are unrelated to migration are partially unexpected, shifting the view of this protein complex's physiological role to other cell biological processes, e.g. regulation of cell proliferation.

Limitations:

The limitations of the study are detailed in the five major points listed above. The study accumulates many experiments that characterize the phenotype of Arpc4-depleted cells, showing signs of DNA damage in Langerhans cells and cultures of BMDCs. How the Arp2/3 complex would mechanistically mediate the observed effects on DNA damage and repairs have not been addressed. It also remains open whether this is due to the effects of the Arp2/3 complex in the nucleus or the cytosol, which would be biologically extremely important to understand. Above that, there are some discrepancies regarding the phenotype of the BMDC model, which does neither entirely match the Langerhans cell phenotype in the tissue (reduced proliferation, LC derive from different progenitors), nor other endogenous DC populations, which should also derive from similar progenitors.

Audience and reviewer background:

In its current form, the manuscript will already be of interest for several research fields: Langerhans cell and dendritic cell homeostasis, immune cell trafficking, actin and cytoskeleton regulation in immune cells, physiological role of actin-regulating proteins. My own field of expertise is immune cell trafficking in mouse models, leukocyte migration and cytoskeletal regulation. I cannot judge the analysis and clustering of the bulk RNA sequencing data.

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Referee #2

Evidence, reproducibility and clarity

Summary:

• This is a study in experimental mice employing both in vitro and, importantly, in vivo approaches. EPIDERMAL LANGERHANS CELLS serve as a paradigm for the maintenance of homeostasis of myeloid cells in a tissue, epidermis in this case. In addition to well known functions of the ACTIN NETWORK in cell migration, chemotaxis, cell adherence and phagocytosis the authors reveal a critical function of actin networks in the survival of cells in their home tissue.

• Actin-related proteins (Arp), specifically here the Arp2/3 complex, are necessary to form the filamentous actin networks. The authors use conditional knock-out mice where Arpc4 (an essential component of the Arp2/3 complex) is deleted under the control of CD11c, the most prominent dendritic cell marker which is also expressed on Langerhans cells. In normal mice, epidermal Langerhans cells reside in the epidermis virtually life-long. They initially settle the epidermis around and few days after birth an establish a dense network by a burst of proliferation and then they "linger on" by low level maintenance proliferation. In the epidermis of Arpc4 knock-out mice Langerhans cells also start off with this proliferative burst but, strikingly, they do not stay but are massively reduced by the age of 8-12 weeks.

• The analyses of this decline revealed that

a) the shape (number of nuclear lobes) and integrity of cell nuclei was compromised; they were fragile and ruptured to some degree when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

b) DNA damage, as detected by staining for gamma-H2Ax or 53BP1 accumulated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

c) recruitment of DNA repair molecules was inhibited when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

d) gene signatures of interferon signaling and response were increased when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

e) in vivo migration of dendritic cells and Langerhans cells from the skin to the draining lymph nodes in an inflammatory setting (FITC painting of the skin) was impaired when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing;

f) the persistence of the typical dense network of Langerhans cells in the epidermis, created by proliferation shortly after birth, is abrogated when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing. Importantly, this was not the case for myeloid cell populations that settle a tissue without needing that initial burst of proliferation. For instance, numbers of colonic macrophages were not affected when Arpc4 was knocked out, i.e., the Arp2/3 complex was missing.

• Thus, the authors conclude that the Arp2/3 complex is essential by its formation of actin networks to maintain the integrity of nuclei and ensure DNA repair thereby ascertaining the maintenance proliferation of Langerhans cells and, as the consequence, the persistence of the dense epidermal netowrk of Langerhans cells.

• Up-to-date methodology from the fields of cell biology and cellular immunology (cell isolation from tissues, immunofluorescence, multiparameter flow cytometry, FISH, "good old" - but important - transmission electronmicroscopy, etc.) was used at high quality (e.g., immunofluorescence pictures!). Quantitative and qualitative analytical methods were timely and appropriate (e.g., Voronoi diagrams, cell shape profiling tools, Cre-lox gene-deletion technology, etc.). Importantly, the authors used a clever method, that they had developed several years ago, namely the analysis of dendritic cell migration in microchannels of defined widths. Molecular biology methods such as RNAseq were also employed and analysed by appropriate bioinformatic tools.

Major comments:

• ARE THE KEY CONCLUSIONS CONVINCING? Yes, they are.

• SHOULD THE AUTHORS QUALIFY SOME OF THEIR CLAIMS AS PRELIMINARY OR SPECULATIVE, OR REMOVE THEM ALTOGETHER? No, I think it is ok as it stands. The authors are wording their claims and conclusions not apodictically but cautiously, as it should be. They point out explicitely which lines of investigations they did not follow up here.

• 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. I think that the here presented experimental evidence suffices to support the conclusions drawn. No additional experiments are necessary.

• 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. Not applicable.

• ARE THE DATA AND THE METHODS PRESENTED IN SUCH A WAY THAT THEY CAN BE REPRODUCED? Yes, they are.

• ARE THE EXPERIMENTS ADEQUATELY REPLICATED AND STATISTICAL ANALYSIS ADEQUATE? Yes.

Minor comments:

• SPECIFIC EXPERIMENTAL ISSUES THAT ARE EASILY ADDRESSABLE. None

• ARE PRIOR STUDIES REFERENCED APPROPRIATELY? Essentially yes. Regarding the reduction / loss of the adult epidermal Langerhans cell network, it may be of some interest to also refer to / discuss to another one of the few examples of this phenomenon. There, the initial burst of proliferation is followed by reduced proliferation and increased apoptosis when a critical member of the mTOR signaling cascade is conditionally knocked out (Blood 123:217, 2014).

• ARE THE TEXT AND FIGURES CLEAR AND ACCURATE? Yes they are. Figures are well arranged for easy comprehension.

• DO YOU HAVE SUGGESTIONS THAT WOULD HELP THE AUTHORS IMPROVE THE PRESENTATION OF THEIR DATA AND CONCLUSIONS?

• Materials & Methods. The authors write, regarding flow cytometry of epidermal cells: "Briefly, 1cm2 of back skin from 8-14 weeks old female wild-type and knockout littermates was dissociated in 0.25 mg/mL Liberase (Sigma, cat. #5401020001) and 0.5 mg/mL DNase (Sigma, cat.#10104159001) in 1 mL of RPMI (Sigma) and mechanically disaggregated in Eppendorf tubes, FOLLOWED BY INCUBATED for 2 h at 37 {degree sign}C." Followed by what?

• Materials & Methods. BMDC electronmicroscopy. What is "IF". Please specify.

• RESULTS in gene expression analyses. The authors observe some increase in apoptosis (as detected by cleaved-Caspase-3 staining). Is this observation in immunofluorescence also evident in the RNAseq data (where the IFN changes were seen), i.e., in Figure 5.

• Figure 7 F and G. Perhaps the authors may want to swap upper and lower panels in F or G, so that macrophage FACS plots and bar graphs are in the same row - ob, obiously, DC plots and bars likewise.

• Figure 7H. "Gating strategy in ArpC4WT Lung (previously gated in Live CD45+ cells)" - The lower row is knock-out, not WT. This is indicated correctly in the legand, but in the figure both rows are labeled as WT.

• The reference by Park et al. 2021 is missing in the list.

• Figure 1D. Sure, the bar graphs are meant to say "CD11c"? The FACS plots show "CD11b".

• As to cDC1. In Figure 1D the FACS plot shows an absence of CD103+ cDC1 cells. In contrast, In Figure 7A-left side panel, there is not difference in cDC1 cells between WT and KO mice. Is therefore the flow cytometry plot in Figure 1D not representative regarding cDC1 cells? Correct?

Significance

• DESCRIBE THE NATURE AND SIGNIFICANCE OF THE ADVANCE (E.G. CONCEPTUAL, TECHNICAL, CLINICAL) FOR THE FIELD. This is a conceptual advance. It adds a big step to our understanding of how immune cells in tissues (which all come from the bone marrow or are seeded before birth from embryonal hematopoietic organs such as yolk sac and fetal liver) can remain resident in these tissues. For cell types such as Langerhans cells, which establish their final population density within their tissues of residence, the presented finding convincingly buttress the role of proliferation and thereby the role for the actin-related protein complex 2/3 (Arp2/3).

• PLACE THE WORK IN THE CONTEXT OF THE EXISTING LITERATURE (PROVIDE REFERENCES, WHERE APPROPRIATE). While we know much about actin-related proteins (Arp), as correctly cited by the authors, this knowledge is derived mostly from in vitro studies. The submitted study translates the findings to an in vivo setting for the first time.

• STATE WHAT AUDIENCE MIGHT BE INTERESTED IN AND INFLUENCED BY THE REPORTED FINDINGS. Skin immunologists foremost, but these findings are of interest to the entire community of immunologists, but also cell biologists.

• DEFINE YOUR FIELD OF EXPERTISE. My expertise is in skin immunology, in particular skin dendritic cells including Langerhans cells.

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Referee #1

Evidence, reproducibility and clarity

Summary:

• The manuscript by Delgado et al. reports the role of the actin remodeling Arp2/3 complex in the biology of Langerhans cells, which are specialized innate immune cells of the epidermis. The study is based on a conditional KO mouse model (CD11cCre;Arpc4fl/fl), in which the deletion of the Arp2/3 subunit ArpC4 is under the control of the myeloid cell specific CD11c promoter.

• In this model, the assembly of LC networks in the epidermis of ear and tail skin is preserved when examining animals immediately after birth (up to 1 week). Subsequently however LCs from ArpC4-deleted mice start displaying morphological aberrations (reduced elongation and number of branches at 4 weeks of age). Additionally, a profound decline in LC numbers is reported in the skin of both the ear and tail of young adult mice (8-10 weeks).

• To explore the cause of such decline, the authors then opt for the complementary in vitro study of bone-marrow derived DCs, given the lack of a model to study LCs in vitro. They report that ArpC4 deletion is associated with aberrantly shaped nuclei, decreased expression of the nucleoskeleton proteins Lamin A/C and B1, nuclear envelop ruptures and increased DNA damage as shown by γH2Ax staining. Importantly, they provide evidence that the defects evoked by ArpC4 deletion also occur in the LCs in situ (immunofluorescence of the skin in 4-week old mice).

• Increased DNA damage is further documented by staining differentiating DCs from ArpC4-deleted mice with the 53BP1 marker. In parallel, nuclear levels of DNA repair kinase ATR and recruitment of RPA70 (which recruits ATR to replicative forks) are reduced in the ArpC4-deleted condition. In vitro treatment of DCs with the topoisomerase II inhibitor etoposide and the Arp2/3 inhibitor CK666 induce comparable DNA damage, as well as multilobulated nuclei and DNA bridges. The authors conclude that the ArpC4-KO phenotype might stem, at least in part, from a defective ability to repair DNA damages occurring during cell division.

• The study in enriched by an RNA-seq analysis that points to an increased expression of genes linked to IFN signaling, which the authors hypothetically relate to overt activation of innate nucleic acid sensing pathways.

• The study ends by an examination of myeloid cell populations in ArpC4-KO mice beyond LCs. Skin cDC2 and cDC2 subsets display skin emigration defects (like LCs), but not numerical defects in the skin (unlike LCs). Myeloid cell subsets of the colon are also present in normal numbers. In the lungs, interstitial and alveolar macrophages are reduced, but not lung DC subsets. Collectively, these observations suggest that ArpC4 is essential for the maintenance of myeloid cell subsets that rely on cell division to colonize or to self-maintain within their tissue of residency (including LCs).

Major comments:

1. ArpC4 and Arp2/3 expression

The authors argue that LCs from Arpc4KO mice should delete the Arpc4 gene in precursors that colonize the skin around birth. It would be important to show it to rule out the possibility that the lack of phenotype (initial seeding, initial proliferative burst) in young animals (first week) could be related to an incomplete deletion of ArpC4 expression. Also important would be to show what is happening to the Arp2/3 complex in LCs from Arpc4KO mice. In the in vitro studies with DCs, the level of ArpC4 and Arp2/3 deletion at the protein level is also not documented. The authors explain that surface expression of the CD11c marker, which drives Arpc4 deletion, gradually increased during differentiation of DCs: from 50% to 90% of the cells. Does that mean that loss of ArpC4 expression is only effective in a fraction of the cells examined before day 10 of differentiation (e.g. in the RNA-seq analysis)?

1. Intra-nuclear versus extra-nuclear activities of Arp2/3

The authors favor a model whereby intra-nuclear ArpC4 helps maintaining nuclear integrity during proliferation of DCs (and possibly LCs). However, multiple pools of Arp2/3 have been described and accordingly, multiple mechanisms may account for the observed phenotype: i) cytoplasmic pool to drive the protrusions sustaining the assembly of the LC network and its connectivity with keratinocytes ; ii) peri-nuclear pool to protect the nucleus ; iii) Intra-nuclear pool to facilite DNA repair mechanisms e.g. by stabilizing replicative forks (the scenario favored by the authors).

It is recommended that the authors try to gather more supportive data to sustain the intra-nuclear role. Documenting ArpC4 presence in the nucleus would help support the claim. It could be combined with treatments aiming at blocking proliferation in order to reinforce the possibility that a main function of ArpC4 is to protect proliferating cells by favoring DNA repair inside the nucleus.

1. Nuclear envelop ruptures

The nuclear envelop ruptures are not sufficiently documented (how many cells were imaged? quantification?). The authors employ STED microscopy to examine Lamin B1 distribution. The image shown in Figure 4A does not really highlight the nuclear envelop, but rather the entire content. Whether it is representative is questionable. We would expect Lamin B1 staining intensity to be drastically reduced given the quantification shown in Figure 3D. In addition, although the authors have stressed in the previous figure that Arpc4-KO is associated with nucleus shape aberrations, the example shown in Figure 4A is that of a nucleus with a normal ovoid shape.

It is recommended to quantify the ruptures with Lap2b antibodies (or another staining that would better delineate the envelop) in order to avoid the possible bias due to the reduced staining intensity of Lamin B1.

A missing analysis is that of nuclear envelop ruptures as a function of nucleus deformations.

Fig 4B-C: same frequency of Arpc4-KO and WT cells displaying nuclear envelop ruptures in the 4-µm channels; however image show a rupture for the Arpc4-KO and no rupture for the WT cells (this is somehow misleading). Are ruptures similar in Arpc4-KO and WT cells in this condition?

Fig 4D-E: is their a direct link between nuclear envelop ruptures and ƴH2A.X?

Interesting (but optional) would be to understand what is happening to DNA, histones? Is their evidence for leakage in the cytoplasm?

1. RNA seq analysis

The RNA-seq analysis suffers from a lack of direct connection with the rest of the study. The extracted molecular information is not validated nor further explored. It remains very descriptive. The PCA analysis suggests a « more pronounced transcriptomic heterogeneity in differentiating Arpc4KO DCs ». However it seems difficult to make such a claim from the comparison of 3 mice per group. In addition, such heterogeneity is not seen in the more detailed analysis (Fig 5F). The authors claim that « day 10 control and Arpc4KO DCs showed no to very little differences in gene expression, in contrast to cells at days 7-9 of differentiation ». This is not obvious from the data displayed in the corresponding figure. In addition, it is not expected that cells that may take a divergent differentiation path at days 7-9 may would return to a similar transcriptional activity at day 10. A point that is not discussed is that before day 10 of DC differentiation, Arpc4 KO is expected to only occur in about 50% of the cell population. This is expected to impact the RNA-seq analysis. Not all clusters have been exploited (e.g. cluster 3 elevated, cluster 6 partly reduced). I suggest the authors reconsider their analysis and analysis of the RNA-seq analysis (or eventually invest in complementary analysis).

1. What causes the profound numerical drop of LC in the epidermis?

A major open question is what causes the massive drop of LCs. Although differentiating Arpc4KO DCs start accumulating DNA damage upon proliferation, they succeed in progressing through the cell cycle. There is even a slightly elevated expression of cell cycle genes at day 7 of differentiation in the DC model. Only a trend for increased apoptosis is observed in ear and tail skin. It would be important to provide complementary data documenting increased death (or aberrant emigration?) of LCs in the 4-8 week time window.

1. Functional consequences

Although the study reports novel aspects of LC biology, the consequence of ArpC4 deletion for skin barrier function and immunosurveillance are not investigated. It would seem very relevant to test how this model copes with radiation, chemical and/or microorganism challenges.

Minor comments:

1. Figure 1D

Gating strategy: twice the same empty plots. The content seems to be missing... Does this need to be shown in the main figure?

1. Figure 2

Best would be to keep same scale to compare P1 and P7 (tail skin, figure 2A)

Overlay of Ki67 and MHC-II does not allow to easily visualize the double-positive cells (Fig 2C)

Quality of Ki67 staining different for Arpc4-KO (less intense, less focused to the nuclei): a technical issue or could that reflect something?

Fig 2C: Panels mounted differently for ear and tail skin (different order to present the individual stainings, Dapi for tail skin only).

1. LC branch analysis (Fig 1 and 2)

While Fig 1 indicates that ear skin LCs form in average twice as few branches as tail skin LCs (3-4 versus 8-9 branches per cell), Fig 2 shows the opposite (10-12 versus 6-7 branches per cell). Is this due to a very distinct pattern between the 2 considered ages (4 weeks versus 8-10 weeks)? Could the author double-check that there is no methodological bias in their analysis?

1. Fig 3 E-G

How many animals were examined (n=5)? Reproducible accros animals? Why was it done with 4-week animals (phenotype not complete? Event occurring before loss in numbers...)

Staining Lamin A/C globally more intense in the Arpc4-KO epidermis (also seems to apply to the masks corresponding to the LCs). Surprising to see that the quantification indicates a major drop of Lamin A/C intensity in the LCs.

1. Legend Fig 4D replace confocal microscopy by STED microscopy

2. Figure 4F

Intensity/background of γH2Ax staining very distinct between the 2 micrographs shown for WT and Arpc4-KO epidermis.

1. Figure 7C, F, H

Gating strategies: would be better to harmonize the style of the plots (dot plots and 2 types of contour plots have been used...)

1. Figure 7H

Legend of lower gating strategy seems to be wrong (KO and not WT).

Significance

Strengths: the general quality of the manuscript is high. It is very clearly written and it contains a very detailed method section that would allow reproducing the reported experiments. This work entails a clear novelty in that it represents the first investigation of the role of ArpC4 in LCs. It opens an interesting perspective about specific mechanisms sustaining the maintenance of myeloid cell subsets in peripheral tissues. This work is therefore expected to be of interest for a large audience of cellular immunologists and beyond. Challenging skin function with an external trigger would lift the relevance for a even wider audience (see main point 6).

Limitations: in its current version the manuscript suffers from a lack of solidity around a few analysis (see main points on ArpC4 and Arp2/3 protein expression, nuclear envelop rupture analysis,...). It also tends to formulate a narrative centered on the ArpC4 intra-nuclear function that is not definitely proven.

The field of expertise of this reviewer is: cellular immunology and actin remodeling.

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Reply to the reviewers

Revision Plan

June 28, 2025

Manuscript number: RC-2025-02982

Corresponding author(s): Babita Madan, Nathan Harmston, David Virshup

General Statements In Wnt signaling, the relative contributions of ‘canonical (β-catenin dependent) and non- canonical (β-catenin independent) signaling remains unclear. Here, we exploited a unique and highly robust in vivo system to study this. Our study is therefore the first comprehensive analysis of the β-catenin independent arm of the Wnt signaling pathway in a cancer model and illustrates how a combination of cis-regulatory elements can determine Wnt-dependent gene regulation.

We are very pleased with the reviews; it appears we communicated our goal and our findings clearly, and in general the reviewers felt the study provided important information, was well planned and the results were “crystal clear”.

While more experiments could strengthen and extend the results, we feel our results are already very robust due to the use of multiple replicates in the in vivo system.

The Virshup lab in Singapore closed July 1, 2025 and so additional wet lab studies are not feasible.

1. 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.

Below we address the points raised by the reviewers:

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

…

The article has the merit of addressing a yet-unsolved question in the field (if beta-catenin can also repress genes) that only a limited number of studies has tried to tackle, and provides useful datasets for the community. The system employed is elegant, and the PORCN-inhibition bypassed by a ____constitutively active beta-catenin is clean and ingenious. The manuscript is clearly written.

We thank the reviewers for their kind comments on the importance of the data. Our orthotopic model provides the opportunity to exploit robust Wnt regulated gene expression in a more responsive microenvironment than can be achieved in cell culture and simple flank xenograft models.

Here we propose a series of thoughts and comments that, if addressed, would in our opinion improve the study and its description.

1) We wonder why a xenograft model is necessary to induce a robust WNT response in these cells.

The authors describe this set-up as a strength, as it is supposed to provide physiological relevance, yet it is not clear to us why this is the case.

We welcome the opportunity to expand on our choice of an orthotopic xenograft model. It has been long established that cancer cells behave differently in different in vivo locations (Killion et al., 1998). Building on this, we confirmed this in our system that identical pancreatic cancer cells treated with the same PORCN inhibitor had very different responses in vitro, in the flank and in their orthotopic environment (Madan et al., 2018). To quote from our prior paper, “Looking only at genes decreasing more than 1.5-fold at 56 hours, we would have missed 817/1867 (44%) genes using a subcutaneous or 939/1867 (50%) using an in vitro model. Thus, the overall response to Wnt inhibition was reduced in the subcutaneous model and further blunted in vitro. An orthotopic model more accurately represents real biology.

The reason for this is presumably the very different orthotopic microenvironment, including tissue appropriate stroma-tumor, vascular-tumor, lymphatic-tumor, and humoral interactions.

Moreover, as the authors homogenize the tumour to perform bulk RNA-seq, we wonder whether they are not only sequencing mRNA from the cancer cells but also from infiltrating immune cells and/or from the surrounding connective tissue.

In experiments generating RNA-seq data from xenograft models, the resulting sequences can originate from either human (graft) or mouse (host). In order to account for this, following standard practice, we filtered reads prior to alignment using Xenome (Conway et al., 2012). We have added additional text to the methods to highlight this step in our pipeline.

2) If, as the established view implies, Wnt/beta-catenin only leads to gene activation, pathway

inhibition would free up the transcriptional machinery - there is evidence that some of its constituents are rate-limiting. The free machinery could now activate some other genes: the net effect observed would be their increased transcription upon Wnt inhibition, irrespective of beta-catenin's presence. Could this be considered as an alternative explanation for the genes that go up in both control and bcat4A lines upon ETC-159 administration? This, we think, is in part corroborated by the absence of enrichment of biological pathways in this group of genes. The genes that are beta-catenin-dependent and downregulated (D&R) are obviously not affected by this alternative explanation.

This is an interesting suggestion, and we will incorporate this thought into our discussion of potential mechanisms.

3) The authors mention that HPAF-II are Wnt addicted. Do they die upon ETC-159 administration, and is this effect rescued by exogenous WNT addition?

We and several others have previously reported that Wnt-addicted cells differentiate and/or senesce upon Wnt withdrawal in vivo but not in vitro. This is related to the broader changes in gene expression in the orthotopic tumors. The effect of PORCN inhibition has been demonstrated by us and others and is rescued by Wnt addition, downstream activation of Wnt signaling by e.g. APC mutation, and, as we show here, stabilized β-catenin.

4) Line 120: the authors write about Figure 1C: "This demonstrates that the growth of β-cat4A cells in vitro largely requires Wnts to activate β-catenin signaling." The opposite is true: control cells require WNT and form less colony with ETC159, while β-cat4A are independent from Wnt secretion.

We appreciate the reviewer pointing out our mis-statement. This error has now been corrected in the revised manuscript.

5) Lines 226-229: "The β-catenin independent repressed genes were notably enriched for motifs bound by homeobox factors including GSC2, POU6F2, and MSGN1. This finding aligns with the known role of non-canonical Wnt signaling in embryonic development" This statement assumes that target genes, or at least the beta-catenin independent ones, are conserved across tissues, including developing organs. This contrasts with the view that target genes in addition to the usual suspects (e.g., AXIN2, SP5 etc.) are modulated tissue-specifically - a view that the authors (and in fact, these reviewers) appear to support in their introduction.

We agree with the reviewer that a majority of Wnt-regulated genes are tissue specific. Indeed, the β-catenin independent Wnt-repressed genes may also be tissue specific. In other tissues, we speculate that other β-catenin independent Wnt-repressed genes may also have homeobox factor binding sites as well and so the general concept remains valid. We do not have sufficient data in other tissues to resolve this issue.

7) The luciferase and mutagenesis work presented in Figure 5 are crystal-clear. One important aspect that remains to be clarified is whether beta-catenin and/or TCF7L2 directly bind to the NRE sites. Or do the authors hypothesize that another factor binds here? We suggest the authors to show TCF7L2 binding tracks at the NRE/WRE motifs in the main figures.

A major question of the reviewers was, can we provide additional evidence that the NRE is bound by LEF/TCF family members. Our initial analysis of more datasets indicates TCF7L2 peaks are enriched on NREs in Wnt-β-catenin responsive cell lines like HCT116 and PANC1. These analyses appear to further support the model that the NRE binds TCF7L2, but we fully agree these analyses can neither prove nor disprove the model.

In our revision, we will analyze additional cut and run datasets as suggested and look at the HEPG2 datasets suggested by reviewer 1. We are concerned about tissue specificity as some of the genes are not expressed in e.g. HEPG2 or HEK293 cells where datasets are available. However, our data continues to support a functional role for the NRE in the modulation of β-catenin regulated genes. The best analysis would be more ChIP-Seq or Cut and Run assays on tissues, not cells, but these studies are beyond what we can do.

What about other TCF/LEFs and beta-catenin? Are there relevant datasets that could be explored to test whether all these bind here during Wnt activation?

As above, We will analyze additional ChIP and Cut & Run datasets to address this question looking at β-catenin and other LEF/TCF family members. We also reflect on the fact that ChIP-Seq does not necessarily imply that the targeted factor (e.g.,TCF7L2) is bound in the target site in all the cells.

The repression might be mediated by beta-catenin partnering with other factors that bind the NRE even by competing with TCF7L2.

We appreciate the insightful comments and now incorporate this into our discussion.

8) In general, while we greatly appreciate the github page to replicate the analysis, we feel that the methods' description is lacking, both concerning analytical details (e.g., the cutoff used for MACS2 peak calling) or basic experimental planning (e.g, how the luciferase assays were performed).

We thank reviewers for the suggestions and will add further details regarding the analysis

and experimental planning in the method sections.

9) The paper might benefit from the addition of quality metrics on the RNA-seq. Interesting for example would be to see a PCA analysis - as a more unbiased approach - rather than the kmeans clustering.

We have this data and will add it to the revised manuscript.

10) It seems that in Figure 3A the clusters are mislabelled as compared to Figure 3B and Figure 1. Here the repressor clusters are labelled DR5, DR6 and DN7 whereas in the rest of the paper they are labelled DR1, DR2 and DN1.

Thank you for pointing out this issue. This has now been corrected in Figure 3.

11) The siCTNNB1 in Figure 5E is described to be a significant effect in the text whereas in Figure 5E this has a p value of 0.075.

Thank you for pointing out the p value did not cross the 0.05 threshold. We have modified the text to remove the word ‘significant’.

12) Line 396: 'Here we confirm and extend the identification of a TCF-dependent negative regulatory element (NRE), where beta-catenin interacts with TCF to repress gene expression'. We suggest caution in stating that beta-catenin and TCF directly repress gene expression by binding to NRE. In the current state the authors do not show that TCF & beta-catenin bind to these elements. See our previous point 7.

We appreciate the suggestion of the reviewers. We will be more cautious in our interpretation.

Further suggestions - or food for thoughts:

13) A frequently asked question in the field concerns the off-target effects of CHIR treatment as opposed to exposure to WNT ligands. CHIR treatment - in parallel to bcat4A overexpression - would allow the authors to delineate WNT independent effects of CHIR treatment and settle this debate.

We thank the reviewers for suggesting this interesting experiment to sort out the non- Wnt effects of GSK3 inhibition. Such a study would require a new set of animal experiments and a different analysis; we think this is beyond the scope of this manuscript.

14) We think that Figure 4C could be strengthened by adding more public TCF-related datasets (e.g., from ENCODE) to confirm the observation across datasets from different laboratories. In particular, the HEPG2 could possibly be improved as there is an excellent TCF7L2 dataset available by ENCODE.

Many more datasets are easily searchable through: https://www.factorbook.org/.

As above, we will analyze the HEPG2 dataset. We plan on updating Fig 4 with data from analysis from different datasets such as (Blauwkamp et al., 2008; Zambanini et al., 2022).

15) The authors show that there is no specific spacing between NREs and WREs. This implies that it is not likely that TCF7L2 recognizes both at the same time through the C-clamp. Do the authors think that there might be a pattern discernible when comparing the location of WRE and NRE in relation to the TCF7L2 ChIP-seq peak summit? This would allow inferring whether TCF7L2 more likely directly binds the WRE (presumably) and if the NRE is bound by a cofactor.

This is an interesting suggestion and we will conduct this analysis as suggested on available datasets (as the result may be different in different tissue types with varying degrees of Wnt/β-catenin signaling).

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

Overall, the study provides a solid framework for understanding noncanonical transcriptional ____outputs of Wnt signaling in a cancer context. The majority of the conclusions are well supported by the data. However, there are a few substantive points that require clarification before the manuscript is ready for publication.

Major Comments

The authors' central claim-that their findings represent a comprehensive analysis of the β-catenin- independent arm of Wnt signaling and uncover a "cis-regulatory grammar" governing Wnt-dependent gene activation versus repression-is overstated based on the presented data.

We appreciate the reviewers concern and will temper our language.

Specifically:

• Figure 3B identifies TF-binding motifs enriched among different Wnt-responsive gene clusters, but the authors only functionally investigate the role of NRE in β-catenin-dependent repression, particularly in the context of TCF motif interaction.

• To support a broader claim regarding cis-regulatory grammar, additional analyses are required:

o What is the distribution of NREs across all clusters? Are they exclusive to β-catenin-dependent repressed clusters, or more broadly present?

The distribution of the NREs is a statistically significant enrichment; they are observed in the repressed clusters more frequently than expected by chance alone, but they are present elsewhere as well. We have tempered our language around the cis-regulatory grammar.

o Do NREs interact with other enriched motifs beyond TCF? Is this interaction specific to repression or also involved in activation?

This is an interesting question beyond the scope of this analysis. Our dataset uses multiple interventions; The NREs may interact with other motifs but we would need more transcriptional analysis data with biological intervention to assess this.

o A more comprehensive analysis of cis-element combinations is needed to draw conclusions about their collective influence on gene regulation across clusters.

We agree; This would be a great question if we had TCF binding data in our orthotopic xenograft model. It’s a dataset we do not have, nor do we have the resources to pursue this.

Other important clarifications:

• The use of the term "wild-type" to describe HPAF-II cells is potentially misleading. These cells are not genetically wild-type and harbor multiple oncogenic alterations.

Thank you for pointing this out. We will use the word “parental” in the text

• The manuscript does not clearly present the kinetics of Wnt target downregulation upon ETC-159 treatment of HPAF-II cells. Understanding whether repression mirrors activation dynamics (e.g., delay or persistence of Wnt effects) is essential to interpreting the system's temporal behavior.

We previously addressed the temporal dynamics of activation and repression in our more comprehensive time course papers (Harmston et al., 2020; Madan et al., 2018); there are differences in the dynamics that are difficult to tease out in this new dataset as the density of time points is less. Having said that, we will compare the time course and annotate the sets of genes identified in this current study with the data from our original study to provide more information on the temporal dynamics of this system.

Minor Comment

• The statement in Figure 1C (lines 119-120) that "growth of β-cat4A cells in vitro largely requires Wnts to activate β-catenin signaling" is inconsistent with the data. As the β-cat4A allele encodes a constitutively active form of β-catenin, Wnts should not be required. Please revise this conclusion for clarity.

We thank the reviewers for pointing out this mis-statement. We have corrected this.

Reviewer #2 (Significance (Required)):

This study offers a systematic classification of Wnt-responsive gene expression dynamics, differentiating between β-catenin-dependent and -independent mechanisms. The insights into temporal expression patterns and the potential role of the NRE element in transcriptional repression add depth to our understanding of Wnt signaling. These findings have relevance for developmental biology, stem cell biology, and cancer research-particularly in understanding how Wnt-mediated repression may influence tumor progression and therapeutic response.

Nice review; thank you.

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

… The work advances understanding of Wnt mediated repression via cis regulatory grammar.

Major Concerns

1) Statistical thresholds and clustering - The criteria for classifying β catenin-dependent versus - independent genes rely on FDR cutoffs above or below 0.1. If the more stringent cutoff of 0.05 was used, how many genes would still be considered Wnt regulated?

We can readily address this in a revised manuscript.

2) Validation of selected β catenin-dependent and -independent Wnt target genes - While the authors identify β catenin-dependent and -independent Wnt target genes (4 selected genes from different clusters in Fig.2), RT-qPCR based validation of Axin2 has been performed in Fig. S3. Authors should also validate other 3 genes as well.

We had considered performing qPCR to re-validate some of our gene-expression changes but qPCR analyses is intrinsically more error prone than RNAseq, and we believe the literature shows that qPCR from the same samples will not add any extra utility. Previous studies that have examined this question have reported excellent correlation between the RNAseq and pPCR (Asmann et al., 2009; Griffith et al., 2010; Wu et al., 2014).

3) NRE mechanistic insight - The most important contribution of this manuscript is the extension of the importance of the NRE motif in Wnt regulated enhancers. But the mutagenesis data provided is insufficient to conclusively nail down that the NREs are responsible for the repression. The effects in the synthetic reporters in Fig. 4D are small - it's not clear that there is much activity in the MimRep to be repressed by the NREs. The data in Fig. 5 is a better context to test the importance of the NREs, but the authors use deletion analysis which is too imprecise and settle for single nucleotide mutants in individual NREs in the ABHD11-AS1 reporter. In the Axin2 report, they mutate sequences outside of the NRE. It's too inconsistent. They should mutate 3 or 4 positions within the NRE in BOTH motifs in the context of the ABHD11-AS1 reporter. Same for the Axin2 reporter.

We feel our analysis, coupled with the Kim paper (Kim et al., 2017), support the role of the NRE. We agree that more data is always desirable, but in our current circumstances are we cannot add additional wetlab experiments.

Regarding Figure 4D, this is a synthetic system lacking the endogenous elements in the promoter. We agree with the reviewer that the effect is small but we would also like to point out that adding the well-established 2WRE in front of the MinRep increased the transcription activity to 1.5 fold, which is of similar magnitude change of the 2NRE deceasing the transcriptional activity 1/1.5 = 0.6.

In Kim et al, it was shown that mutating the 11st nucleotide of the NRE motif showed the strongest effect, so we followed their lead in only mutated the 11st nucleotide in ABHD11- AS1 NRE.

As for the putative NRE sequence present in AXIN2 promoter, its downstream sequence is polyT (__GTGTTTTTTTT__TTTTTTTTTT), if we only mutate 11st nucleotide to G/C, we could create similar sequence to NRE, so we mutated sequences outside of the NRE to fully disrupt it.

4) Even if the mutagenesis is done more completely, the results simply replicate that of the Goentoro group. In Kim et al 2017, they provide suggestive (not convincing) evidence that TCFs directly bind to the NRE. The authors of this manuscript should explore that in more detail, e.g., can purified TCF bind to the NRE sequence? Can the authors design experiments to directly test whether beta-catenin is acting through the NRE - their data currently only demonstrates that the NRE provide a negative input to the reporters - that's an important mechanistic difference.

We point out that our minimal reporter studies with the NRE showed a repressive effect in HCT116 (colorectal cancer cells with stabilized β-catenin) but not HT1080 (sarcoma cells with low Wnt) supporting the importance of β-catenin acting through the NRE (Figs. 4D, 4E).

We fully agree with the reviewers that additional study of TCF interaction with the NRE would be of value. While EMSA and culture-based ChIP assays would be of some value, the best study should be done in vivo where the system is most robust. We are not in a position to do these studies, but we will add in a discussion of this as a limitation of the current study.

5) In vertebrates, some TCFs are more repressive than others and TLEs have been implicated in repressive. Exploring these factors in the context of the NRE would increase the value of this story.

This is an interesting idea but beyond the scope of the current manuscript. It is likely this would be dependent on tissue specific expression, local expression levels, and local binding of co-factors. As we look at other TCF members in other datasets we may be able to address this. Further wetlab experiments are beyond the scope of this work.

**Referees cross-commenting**

I respectfully disagree that the luciferase assays are sufficient. Using deletion analysis to understand the function of specific binding sites is insufficient and the more specific mutations of NREs are incomplete. Regarding this paper extending our knowledge of direct transcriptional repression by Wnt/bcat signaling, I don't agree that it adds much - there are numerous datasets where Wnt signaling activates and represses genes - the trick is determining whether any of the repressed genes are the result and direct regulation by TCF/bcat. They don't explore that. The main finding is an extension of the work by Lea Goentoro on the importance of the NRE motif, but they don't address whether TCF directly associates with this sequence. Goentoro argued in the 2017 paper that it does, but that data is unconvincing to me. Can purified TCF bind the NRE? Without that information (done carefully) this manuscript is very limited.

We respectfully disagree with the reviewer regarding the contribution of this manuscript. There are certainly many datasets looking at Wnt-regulated genes in tissue culture, but these cell-based studies are underpowered to really understand Wnt biology. There are only two papers, ours and Cantú’s, that address Wnt repressed genes in any depth. No prior papers have differentiated β-catenin dependent from β-catenin independent genes before, and certainly not in an orthotopic animal model.

A major impact of our study is the finding that only 10% of Wnt regulated genes are independent of β-catenin, at least in pancreatic cancer. We feel this is a major contribution. We further add to this analysis by re-enforcing/extend the prior evidence on the NRE in humans (and correct the motif sequence!) for Wnt-repressed genes. Our data supports the fine-tuning of the Wnt/β-catenin regulated genes by a cis-regulatory grammar.

Reviewer #3 (Significance (Required)):

Overall, this study advances our understanding of the dual roles of Wnt signaling in gene activation and repression, highlighting the role of the NRE motif. But this is an extension of the original NRE paper (Kim et al 2017) with no mechanistic advance beyond that original work. The transcriptomics in the first part of the manuscript have some value, but similar data sets already exist.

We respectfully but strongly disagree with the reviewer. First, our work examines the NRE in a large-scale in vivo transcriptome dataset, significantly extending the candidate gene approach of Kim et al. Secondly, we disagree with the comment that “similar data sets already exist.” Indeed, reviewer 1 (C. Cantú) specifically pointed out we had addressed an “yet-unsolved question in the field” on whether and how β-catenin repressed genes.

__3. __Description of the revisions that have already been incorporated in the transferred manuscript

To date we have only corrected several typographical errors.

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

We fully agree with the reviewers that additional study of TCF interaction with the NRE would be of value. While EMSA and cell culture-based ChIP assays would be of some modest value, they have already been done in vitro by Kim et al. (Kim et al., 2017) and the best next study should be done in vivo in Wnt-responsive cancers or tissues where the biology is most robust (Madan et al., 2018) . We are not in a position to do these studies, but we will add this into the discussion as a limitation of the current study. We also acknowledge that the NRE may interact with other currently unidentified factors.

Reviewer 1 asked about considering experiments to determine non-Wnt effects of GSK3 inhibitors like CHIR. Such a study, while interesting, would require a new set of animal experiments and a different analysis; we think this is beyond the scope of this manuscript.

Finally, we note that the Virshup lab at Duke-NUS Medical School in Singapore, where these in vivo studies were performed, has closed as of July 1, 2025 and the various lab members have moved on to new adventures. Because of this, we are unable to undertake new wet-lab studies.

Thank you for your consideration,

For the authors,

David Virshup

References:

Asmann YW, Klee EW, Thompson EA, Perez EA, Middha S, Oberg AL, Therneau TM, Smith DI,

Poland GA, Wieben ED, Kocher J-PA. 2009. 3’ tag digital gene expression profiling of human

brain and universal reference RNA using Illumina Genome Analyzer. BMC Genom 10:531–

1. doi:10.1186/1471-2164-10-531

Blauwkamp TA, Chang MV, Cadigan KM. 2008. Novel TCF-binding sites specify transcriptional

repression by Wnt signalling. The EMBO Journal 27:1436–1446. doi:10.1038/emboj.2008.80

Conway T, Wazny J, Bromage A, Tymms M, Sooraj D, Williams ED, Beresford-Smith B. 2012.

Xenome—a tool for classifying reads from xenograft samples. Bioinformatics 28:i172–i178.

doi:10.1093/bioinformatics/bts236

Griffith M, Griffith OL, Mwenifumbo J, Goya R, Morrissy AS, Morin RD, Corbett R, Tang MJ, Hou

Y-C, Pugh TJ, Robertson G, Chittaranjan S, Ally A, Asano JK, Chan SY, Li HI, McDonald H,

Teague K, Zhao Y, Zeng T, Delaney A, Hirst M, Morin GB, Jones SJM, Tai IT, Marra MA.

1. Alternative expression analysis by RNA sequencing. Nat Methods 7:843–847.

doi:10.1038/nmeth.1503

Harmston N, Lim JYS, Arqués O, Palmer HG, Petretto E, Virshup DM, Madan B. 2020.

Widespread Repression of Gene Expression in Cancer by a Wnt/β-Catenin/MAPK Pathway.

Cancer Res 81:464–475. doi:10.1158/0008-5472.can-20-2129

Killion JJ, Radinsky R, Fidler IJ. 1998. Orthotopic models are necessary to predict therapy of

transplantable tumors in mice. Cancer metastasis reviews 17:279–284.

Kim K, Cho J, Hilzinger TS, Nunns H, Liu A, Ryba BE, Goentoro L. 2017. Two-Element

Transcriptional Regulation in the Canonical Wnt Pathway. Current Biology 27:2357-2364.e5.

doi:10.1016/j.cub.2017.06.037

Madan B, Harmston N, Nallan G, Montoya A, Faull P, Petretto E, Virshup DM. 2018. Temporal

dynamics of Wnt-dependent transcriptome reveals an oncogenic Wnt/MYC/ribosome axis. J

Clin Invest 128:5620–5633. doi:10.1172/jci122383

Wu AR, Neff NF, Kalisky T, Dalerba P, Treutlein B, Rothenberg ME, Mburu FM, Mantalas GL,

Sim S, Clarke MF, Quake SR. 2014. Quantitative assessment of single-cell RNA-sequencing

methods. Nat Methods 11:41–46. doi:10.1038/nmeth.2694

Zambanini G, Nordin A, Jonasson M, Pagella P, Cantù C. 2022. A new cut&run low volume-

urea (LoV-U) protocol optimized for transcriptional co-factors uncovers Wnt/b-catenin tissue-

specific genomic targets. Development 149. doi:10.1242/dev.201124

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Referee #3

Evidence, reproducibility and clarity

The authors use a PORCN inhibitor (ETC 159) in an orthotopic RNF43 mutant pancreatic cancer model to distinguish β catenin-dependent from -independent Wnt target genes. They find that ~90% of Wnt regulated genes in this system are β catenin dependent. Approximately half of these genes are activated by Wnt signaling, half repressed. Clustering and functional enrichment link dependent versus independent targets to distinct pathways. They observe enrichment of sequence motifs similar to the 11 bp Negative Regulatory Element (NRE) previously identified by Lea Goentoro's group in the region around the TSS of β catenin-repressed genes. Using reporter constructs, both synthetic and regulatory DNA from Wnt targets (e.g., ABHD11 AS1, AXIN2), they provide evidence that the NREs are a negative input on expression. The work advances understanding of Wnt mediated repression via cis regulatory grammar.

Major Concerns

1. Statistical thresholds and clustering - The criteria for classifying β catenin-dependent versus -independent genes rely on FDR cutoffs above or below 0.1. If the more stringent cutoff of 0.05 was used, how many genes would still be considered Wnt regulated?
2. Validation of selected β catenin-dependent and -independent Wnt target genes - While the authors identify β catenin-dependent and -independent Wnt target genes (4 selected genes from different clusters in Fig.2), RT-qPCR based validation of Axin2 has been performed in Fig. S3. Authors should also validate other 3 genes as well.
3. NRE mechanistic insight - The most important contribution of this manuscript is the extension of the importance of the NRE motif in Wnt regulated enhancers. But the mutagenesis data provided is insufficient to conclusively nail down that the NREs are responsible for the repression. The effects in the synthetic reporters in Fig. 4D are small - it's not clear that there is much activity in the MimRep to be repressed by the NREs. The data in Fig. 5 is a better context to test the importance of the NREs, but the authors use deletion analysis which is too imprecise and settle for single nucleotide mutants in individual NREs in the ABHD11-AS1 reporter. In the Axin2 report, they mutate sequences outside of the NRE. It's too inconsistent. They should mutate 3 or 4 positions within the NRE in BOTH motifs in the context of the ABHD11-AS1 reporter. Same for the Axin2 reporter.
4. Even if the mutagenesis is done more completely, the results simply replicate that of the Goentoro group. In Kim et al 2017, they provide suggestive (not convincing) evidence that TCFs directly bind to the NRE. The authors of this manuscript should explore that in more detail, e.g., can purified TCF bind to the NRE sequence? Can the authors design experiments to directly test whether beta-catenin is acting through the NRE - their data currently only demonstrates that the NRE provide a negative input to the reporters - that's an important mechanistic difference.
5. In vertebrates, some TCFs are more repressive than others and TLEs have been implicated in repressive. Exploring these factors in the context of the NRE would increase the value of this story.

Referees cross-commenting

I respectfully disagree that the luciferase assays are sufficient. Using deletion analysis to understand the function of specific binding sites is insufficient and the more specfic mutations of NREs are incomplete. Regarding this paper extending our knowledge of direct transcriptional repression by Wnt/bcat signaling, I don't agree that it adds much - there are numerous datasets where Wnt signaling activates and represses genes - the trick is determining whether any of the repressed genes are the result and direct regulation by TCF/bcat. They don't explore that. The main finding is an extension of the work by Lea Goentoro on the importance of the NRE motif, but they don't address whether TCF directly associates with this sequence. Goentoro argued in the 2017 paper that it does, but that data is unconvincing to me. Can purified TCF bind the NRE? Without that information (done carefully) this manuscript is very limited.

Significance

Overall, this study advances our understanding of the dual roles of Wnt signaling in gene activation and repression, highlighting the role of the NRE motif. But this is an extension of the original NRE paper (Kim et al 2017) with no mechanistic advance beyond that original work. The transcriptomics in the first part of the manuscript have some value, but similar data sets already exist.

Addressing the major points-especially gaining a deeper mechanistic insight into NRE function-would elevate the manuscript's impact. Major revisions are recommended.

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Referee #2

Evidence, reproducibility and clarity

This manuscript by Liu et al. explores lesser-known aspects of Wnt signaling, particularly focusing on genes that are repressed by β-catenin and those regulated independently of β-catenin. While canonical Wnt signaling is well characterized through the stabilization and nuclear translocation of β-catenin to activate TCF/LEF target genes, the mechanisms underlying gene repression and β-catenin-independent regulation remain relatively underexplored.

The authors leverage the Wnt-addicted HPAF-II cancer cell line, combining PORCN inhibitor (ETC-159) treatment with ectopic expression of a stabilized β-catenin mutant (β-cat4A) in orthotopic xenograft models. Through RNA-sequencing analysis, they systematically identify Wnt-responsive gene clusters that are either dependent or independent of β-catenin stabilization. They further demonstrate that a specific cis-regulatory element, termed the Negative Regulatory Element (NRE), contributes to β-catenin-mediated transcriptional repression.

Overall, the study provides a solid framework for understanding noncanonical transcriptional outputs of Wnt signaling in a cancer context. The majority of the conclusions are well supported by the data. However, there are a few substantive points that require clarification before the manuscript is ready for publication.

Major Comments

The authors' central claim-that their findings represent a comprehensive analysis of the β-catenin-independent arm of Wnt signaling and uncover a "cis-regulatory grammar" governing Wnt-dependent gene activation versus repression-is overstated based on the presented data.

Specifically:

• Figure 3B identifies TF-binding motifs enriched among different Wnt-responsive gene clusters, but the authors only functionally investigate the role of NRE in β-catenin-dependent repression, particularly in the context of TCF motif interaction.
• To support a broader claim regarding cis-regulatory grammar, additional analyses are required:
  • What is the distribution of NREs across all clusters? Are they exclusive to β-catenin-dependent repressed clusters, or more broadly present?
  • Do NREs interact with other enriched motifs beyond TCF? Is this interaction specific to repression or also involved in activation?
  • A more comprehensive analysis of cis-element combinations is needed to draw conclusions about their collective influence on gene regulation across clusters.

Other important clarifications:

• The use of the term "wild-type" to describe HPAF-II cells is potentially misleading. These cells are not genetically wild-type and harbor multiple oncogenic alterations.
• The manuscript does not clearly present the kinetics of Wnt target downregulation upon ETC-159 treatment of HPAF-II cells. Understanding whether repression mirrors activation dynamics (e.g., delay or persistence of Wnt effects) is essential to interpreting the system's temporal behavior.

Minor Comment

• The statement in Figure 1C (lines 119-120) that "growth of β-cat4A cells in vitro largely requires Wnts to activate β-catenin signaling" is inconsistent with the data. As the β-cat4A allele encodes a constitutively active form of β-catenin, Wnts should not be required. Please revise this conclusion for clarity.

Significance

This study offers a systematic classification of Wnt-responsive gene expression dynamics, differentiating between β-catenin-dependent and -independent mechanisms. The insights into temporal expression patterns and the potential role of the NRE element in transcriptional repression add depth to our understanding of Wnt signaling. These findings have relevance for developmental biology, stem cell biology, and cancer research-particularly in understanding how Wnt-mediated repression may influence tumor progression and therapeutic response.

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

Shiyang Liu and colleagues investigate the transcription induced by Wnt/beta-catenin by employing PORCN inhibition (ECT-159, blocking the secretion of WNTs) in the Wnt-addicted HPAF-II cell line. Classical targets, such as AXIN2, are downregulated by PORCN inhibition (as expected), while many other genes are upregulated, suggesting that Wnt/beta-catenin represses them. Overexpression of a GSK3/CK1-insensitive beta-catenin variant leads to the re-established upregulation of AXIN2 and the concomitant repression of the other group of repressed genes, demonstrating that the repression is mediated by beta-catenin. Other genes are repressed (activated by ECT-159) irrespective of the presence of activated beta-catenin, and the authors conclude that they are beta-catenin-independent Wnt-repressed genes. The authors observe that beta-catenin-dependent repressed genes present enrichment, in their promoters, of the Negative Regulatory Element (NRE) previously identified by the Goentoro lab. In elegant Luciferase assays, the authors now confirm that individual NRE elements are causally involved in target gene repression by -catenin. The article has the merit of addressing a yet-unsolved question in the field (if beta-catenin can also repress genes) that only a limited number of studies has tried to tackle, and provides useful datasets for the community. The system employed is elegant, and the PORCN-inhibition bypassed by a constitutively active beta-catenin is clean and ingenious. The manuscript is clearly written.

Here we propose a series of thoughts and comments that, if addressed, would in our opinion improve the study and its description.

1. We wonder why a xenograft model is necessary to induce a robust WNT response in these cells. The authors describe this set-up as a strength, as it is supposed to provide physiological relevance, yet it is not clear to us why this is the case. Moreover, as the authors homogenize the tumour to perform bulk RNA-seq, we wonder whether they are not only sequencing mRNA from the cancer cells but also from infiltrating immune cells and/or from the surrounding connective tissue.
2. If, as the established view implies, Wnt/beta-catenin only leads to gene activation, pathway inhibition would free up the transcriptional machinery - there is evidence that some of its constituents are rate-limiting. The free machinery could now activate some other genes: the net effect observed would be their increased transcription upon Wnt inhibition, irrespective of beta-catenin's presence. Could this be considered as an alternative explanation for the genes that go up in both control and cat4A lines upon ETC-159 administration? This, we think, is in part corroborated by the absence of enrichment of biological pathways in this group of genes. The genes that are beta-catenin-dependent and downregulated (D&R) are obviously not affected by this alternative explanation.
3. The authors mention that HPAF-II are Wnt addicted. Do they die upon ETC-159 administration, and is this effect rescued by exogenous WNT addition?
4. Line 120: the authors write about Figure 1C: "This demonstrates that the growth of β-cat4A cells in vitro largely requires Wnts to activate β-catenin signaling." The opposite is true: control cells require WNT and form less colony with ETC159, while β-cat4A are independent from Wnt secretion.
5. Lines 226-229: "The β-catenin independent repressed genes were notably enriched for motifs bound by homeobox factors including GSC2, POU6F2, and MSGN1. This finding aligns with the known role of non-canonical Wnt signaling in embryonic development." This statement assumes that target genes, or at least the beta-catenin independent ones, are conserved across tissues, including developing organs. This contrasts with the view that target genes in addition to the usual suspects (e.g., AXIN2, SP5 etc.) are modulated tissue-specifically - a view that the authors (and in fact, these reviewers) appear to support in their introduction.
6. The luciferase and mutagenesis work presented in Figure 5 are crystal-clear. One important aspect that remains to be clarified is whether beta-catenin and/or TCF7L2 directly bind to the NRE sites. Or do the authors hypothesize that another factor binds here? We suggest the authors to show TCF7L2 binding tracks at the NRE/WRE motifs in the main figures. What about other TCF/LEFs and beta-catenin? Are there relevant datasets that could be explored to test whether all these bind here during Wnt activation? We also reflect on the fact that ChIP-Seq does not necessarily imply that the targeted factor (e.g., TCF7L2) is bound in the target site in all the cells. The repression might be mediated by beta-catenin partnering with other factors that bind the NRE even by competing with TCF7L2.
7. In general, while we greatly appreciate the github page to replicate the analysis, we feel that the methods' description is lacking, both concerning analytical details (e.g., the cutoff used for MACS2 peak calling) or basic experimental planning (e.g, how the luciferase assays were performed).
8. The paper might benefit from the addition of quality metrics on the RNA-seq. Interesting for example would be to see a PCA analysis - as a more unbiased approach - rather than the kmeans clustering.
9. It seems that in Figure 3A the clusters are mislabelled as compared to Figure 3B and Figure 1. Here the repressor clusters are labelled DR5, DR6 and DN7 whereas in the rest of the paper they are labelled DR1, DR2 and DN1.
10. The siCTNNB1 in Figure 5E is described to be a significant effect in the text whereas in Figure 5E this has a p value of 0.075.
11. Line 396: 'Here we confirm and extend the identification of a TCF-dependent negative regulatory element (NRE), where beta-catenin interacts with TCF to repress gene expression'. We suggest caution in stating that beta-catenin and TCF directly repress gene expression by binding to NRE. In the current state the authors do not show that TCF & beta-catenin bind to these elements. See our previous point 7.

Further suggestions - or food for thoughts: 13. A frequently asked question in the field concerns the off-target effects of CHIR treatment as opposed to exposure to WNT ligands. CHIR treatment - in parallel to bcat4A overexpression - would allow the authors to delineate WNT independent effects of CHIR treatment and settle this debate. 14. We think that Figure 4C could be strengthened by adding more public TCF-related datasets (e.g., from ENCODE) to confirm the observation across datasets from different laboratories. In particular, the HEPG2 could possibly be improved as there is an excellent TCF7L2 dataset available by ENCODE. Many more datasets are easily searchable through: https://www.factorbook.org/. 15. The authors show that there is no specific spacing between NREs and WREs. This implies that it is not likely that TCF7L2 recognizes both at the same time through the C-clamp. Do the authors think that there might be a pattern discernible when comparing the location of WRE and NRE in relation to the TCF7L2 ChIP-seq peak summit? This would allow inferring whether TCF7L2 more likely directly binds the WRE (presumably) and if the NRE is bound by a cofactor.

Review by Claudio Cantù and Yorick van de Grift

Why we sign: we believe that peer review should be a transparent dialogue. We strive to be critical but honest and professional, and care that our opinions and criticisms are formulated as if we were meeting the authors in person.

Our expertise lies in the genomics impact of Wnt/beta-catenin activation, and in the search of mechanisms that drive the tissue-specific functions of this pathway across developmental and disease contexts.

Significance

Shiyang Liu and colleagues investigate the transcription induced by Wnt/beta-catenin by employing PORCN inhibition (ECT-159, blocking the secretion of WNTs) in the Wnt-addicted HPAF-II cell line. Classical targets, such as AXIN2, are downregulated by PORCN inhibition (as expected), while many other genes are upregulated, suggesting that Wnt/beta-catenin represses them. Overexpression of a GSK3/CK1-insensitive beta-catenin variant leads to the re-established upregulation of AXIN2 and the concomitant repression of the other group of repressed genes, demonstrating that the repression is mediated by beta-catenin. Other genes are repressed (activated by ECT-159) irrespective of the presence of activated beta-catenin, and the authors conclude that they are beta-catenin-independent Wnt-repressed genes. The authors observe that beta-catenin-dependent repressed genes present enrichment, in their promoters, of the Negative Regulatory Element (NRE) previously identified by the Goentoro lab. In elegant Luciferase assays, the authors now confirm that individual NRE elements are causally involved in target gene repression by -catenin. The article has the merit of addressing a yet-unsolved question in the field (if beta-catenin can also repress genes) that only a limited number of studies has tried to tackle, and provides useful datasets for the community. The system employed is elegant, and the PORCN-inhibition bypassed by a constitutively active beta-catenin is clean and ingenious. The manuscript is clearly written.

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

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Reply to the reviewers

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

PAPS is required for all sulfotransferase reactions in which a sulfate group is covalently attached to amino acid residues of proteins or to side chains of proteoglycans. This sulfation is crucial for properly organizing the apical extracellular matrix (aECM) and expanding the lumen in the Drosophila salivary gland. Loss of Papss potentially leads to decreased sulfation, disorganizing the aECM, and defects in lumen formation. In addition, Papss loss destabilizes the Golgi structures.

In Papss mutants, several changes occur in the salivary gland lumen of Drosophila. The tube lumen is very thin and shows irregular apical protrusions. There is a disorganization of the apical membrane and a compaction of the apical extracellular matrix (aECM). The Golgi structures and intracellular transport are disturbed. In addition, the ZP domain proteins Piopio (Pio) and Dumpy (Dpy) lose their normal distribution in the lumen, which leads to condensation and dissociation of the Dpy-positive aECM structure from the apical membrane. This results in a thin and irregularly dilated lumen.

1. The authors describe various changes in the lumen in mutants, from thin lumen to irregular expansion. I would like to know the correct lumen diameter, and length, besides the total area, by which one can recognize thin and irregular.

We have included quantification of the length and diameter of the salivary gland lumen in the stage 16 salivary glands of control, Papss mutant, and salivary gland-specific rescue embryos (Figure 1J, K). As described, Papss mutant embryos have two distinct phenotypes, one group with a thin lumen along the entire lumen and the other group with irregular lumen shapes. Therefore, we separated the two groups for quantification of lumen diameter. Additionally, we have analyzed the degree of variability for the lumen diameter to better capture the range of phenotypes observed (Figure 1K'). These quantifications enable a more precise assessment of lumen morphology, allowing readers to distinguish between thin and irregular lumen phenotypes.

The rescue is about 30%, which is not as good as expected. Maybe the wrong isoform was taken. Is it possible to find out which isoform is expressed in the salivary glands, e.g., by RNA in situ Hyb? This could then be used to analyze a more focused rescue beyond the paper.

Thank you for this point, but we do not agree that the rescue is about 30%. In Papss mutants, about 50% of the embryos show the thin lumen phenotype whereas the other 50% show irregular lumen shapes. In the rescue embryos with a WT Papss, few embryos showed thin lumen phenotypes. About 40% of the rescue embryos showed "normal, fully expanded" lumen shapes, and the remaining 60% showed either irregular (thin+expanded) or slightly overexpanded lumen. It is not uncommon that rescue with the Gal4/UAS system results in a partial rescue because it is often not easy to achieve the balance of the proper amount of the protein with the overexpression system.

To address the possibility that the wrong isoform was used, we performed in situ hybridization to examine the expression of different Papss spice forms in the salivary gland. We used probes that detect subsets of splice forms: A/B/C/F/G, D/H, and E/F/H, and found that all probes showed expression in the salivary gland, with varying intensities. The original probe, which detects all splice forms, showed the strongest signals in the salivary gland compared to the new probes which detect only a subset. However, the difference in the signal intensity may be due to the longer length of the original probe (>800 bp) compared to other probes that were made with much smaller regions (~200 bp). Digoxigenin in the DIG labeling kit for mRNA detection labels the uridine nucleotide in the transcript, and the probes with weaker signals contain fewer uridines (all: 147; ABCFG, 29; D, 36; EFH, 66). We also used the Papss-PD isoform, for a salivary gland-specific rescue experiment and obtained similar results to those with Papss-PE (Figure 1I-L, Figure 4D and E).

Furthermore, we performed additional experiments to validate our findings. We performed a rescue experiment with a mutant form of Papss that has mutations in the critical rescues of the catalytic domains of the enzyme, which failed to rescue any phenotypes, including the thin lumen phenotype (Figure 1H, J-L), the number and intensity of WGA puncta (Figure 3I, I'), and cell death (Figure 4D, E). These results provide strong evidence that the defects observed in Papss mutants are due to the lack of sulfation.

Crb is a transmembrane protein on the apicolateral side of the membrane. Accordingly, the apicolateral distribution can be seen in the control and the mutant. I believe there are no apparent differences here, not even in the amount of expression. However, the view of the cells (frame) shows possible differences. To be sure, a more in-depth analysis of the images is required. Confocal Z-stack images, with 3D visualization and orthogonal projections to analyze the membranes showing Crb staining together with a suitable membrane marker (e.g. SAS or Uif). This is the only way to show whether Crb is incorrectly distributed. Statistics of several papas mutants would also be desirable and not just a single representative image. When do the observed changes in Crb distribution occur in the development of the tubes, only during stage 16? Is papss only involved in the maintenance of the apical membrane? This is particularly important when considering the SJ and AJ, because the latter show no change in the mutants.

We appreciate your suggestion to more thoroughly analyze Crb distribution. We adapted a method from a previous study (Olivares-Castiñeira and Llimargas, 2017) to quantify Crb signals in the subapical region and apical free region of salivary gland cells. Using E-Cad signals as a reference, we marked the apical cell boundaries of individual cells and calculated the intensity of Crb signals in the subapical region (along the cell membrane) and in the apical free region. We focused on the expanded region of the SG lumen in Papss mutants for quantification, as the thin lumen region was challenging to analyze. This quantification is included in Figure 2D. Statistical analysis shows that Crb signals were more dispersed in SG cells in Papss mutants compared to WT.

A change in the ECM is only inferred based on the WGA localization. This is too few to make a clear statement. WGA is only an indirect marker of the cell surface and glycosylated proteins, but it does not indicate whether the ECM is altered in its composition and expression. Other important factors are missing here. In addition, only a single observation is shown, and statistics are missing.

We understand your concern that WGA localization alone may not be sufficient to conclude changes in the ECM. However, we observed that luminal WGA signals colocalize with Dpy-YFP in the WT SG (Figure 5-figure supplement 2C), suggesting that WGA detects the aECM structure containing Dpy. The similar behavior of WGA and Dpy-YFP signals in multiple genotypes further supports this idea. In Papss mutants with a thin lumen phenotype, both WGA and Dpy-YFP signals are condensed (Figure 5E-H), and in pio mutants, both are absent from the lumen (Figure 6B, D). We analyzed WGA signals in over 25 samples of WT and Papss mutants, observing consistent phenotypes. We have included the number of samples in the text. While we acknowledge that WGA is an indirect marker, our data suggest that it is a reliable indicator of the aECM structure containing Dpy.

Reduced WGA staining is seen in papss mutants, but this could be due to other circumstances. To be sure, a statistic with the number of dots must be shown, as well as an intensity blot on several independent samples. The images are from single confocal sections. It could be that the dots appear in a different Z-plane. Therefore, a 3D visualization of the voxels must be shown to identify and, at best, quantify the dots in the organ.

We have quantified cytoplasmic punctate WGA signals. Using spinning disk microscopy with super-resolution technology (Olympus SpinSR10 Sora), we obtained high-resolution images of cytoplasmic punctate signals of WGA in WT, Papss mutant, and rescue SGs with the WT and mutant forms of Papss-PD. We then generated 3D reconstructed images of these signals using Imaris software (Figure 3E-H) and quantified the number and intensity of puncta. Statistical analysis of these data confirms the reduction of the number and intensity of WGA puncta in Papss mutants (Figure 3I, I'). The number of WGA puncta was restored by expressing WT Papss but not the mutant form. By using 3D visualization and quantification, we have ensured that our results are not limited to a single confocal section and account for potential variations in Z-plane localization of the dots.

A colocalization analysis (statistics) should be shown for the overlap of WGA with ManII-GFP.

Since WGA labels multiple structures, including the nuclear envelope and ECM structures, we focused on assessing the colocalization of the cytoplasmic WGA punctate signals and ManII-GFP signals. Standard colocalization analysis methods, such as Pearson's correlation coefficient or Mander's overlap coefficient, would be confounded by WGA signals in other tissues. Therefore, we used a fluorescent intensity line profile to examine the spatial relationship between WGA and ManII-GFP signals in WT and Papss mutants (Figure 3L, L').

I do not understand how the authors describe "statistics of secretory vesicles" as an axis in Figure 3p. The TEM images do not show labeled secretory vesicles but empty structures that could be vesicles.

Previous studies have analyzed "filled" electron-dense secretory vesicles in TEM images of SG cells (Myat and Andrew, 2002, Cell; Fox et al., 2010, J Cell Biol; Chung and Andrew, 2014, Development). Consistent with these studies, our WT TEM images show these vesicles. In contrast, Papss mutants show a mix of filled and empty structures. For quantification, we specifically counted the filled electron-dense vesicles (now Figure 3W). A clear description of our analysis is provided in the figure legend.

1. The quality of the presented TEM images is too low to judge any difference between control and mutants. Therefore, the supplement must present them in better detail (higher pixel number?).

We disagree that the quality of the presented TEM images is too low. Our TEM images have sufficient resolution to reveal details of many subcellular structures, such as mitochondrial cisternae. The pdf file of the original submission may not have been high resolution. To address this concern, we have provided several original high-quality TEM images of both WT and Papss mutants at various magnifications in Figure 2-figure supplement 2. Additionally, we have included low-magnification TEM images of WT and Papss mutants in Figure 2H and I to provide a clearer view of the overall SG lumen morphology.

Line 266: the conclusion that apical trafficking is "significantly impaired" does not hold. This implies that Papss is essential for apical trafficking, but the analyzed ECM proteins (Pio, Dumpy) are found apically enriched in the mutants, and Dumpy is even secreted. Moreover, they analyze only one marker, Sec15, and don't provide data about the quantification of the secretion of proteins.

We agree and have revised our statement to "defective sulfation affects Golgi structures and multiple routes of intracellular trafficking".

DCP-1 was used to detect apoptosis in the glands to analyze acellular regions. However, the authors compare ST16 control with ST15 mutant salivary glands, which is problematic. Further, it is not commented on how many embryos were analyzed and how often they detect the dying cells in control and mutant embryos. This part must be improved.

Thank you for the comment. We agree and have included quantification. We used stage 16 samples from WT and Papss mutants to quantify acellular regions. Since DCP-1 signals are only present at a specific stage of apoptosis, some acellular regions do not show DCP-1 signals. Therefore, we counted acellular regions regardless of DCP-1 signals. We also quantified this in rescue embryos with WT and mutant forms of Papss, which show complete rescue with WT and no rescue with the mutant form, respectively. The graph with a statistical analysis is included (Figure 4D, E).

WGA and Dumpy show similar condensed patterns within the tube lumen. The authors show that dumpy is enriched from stage 14 onwards. How is it with WGA? Does it show the same pattern from stage 14 to 16? Papss mutants can suffer from a developmental delay in organizing the ECM or lack of internalization of luminal proteins during/after tube expansion, which is the case in the trachea.

Dpy-YFP and WGA show overlapping signals in the SG lumen throughout morphogenesis. Dpy-YFP is SG enriched in the lumen from stage 11, not stage 14 (Figure 5-figure supplement 2). WGA is also detected in the lumen throughout SG morphogenesis, similar to Dpy. In the original supplemental figure, only a stage 16 SG image was shown for co-localization of Dpy-YFP and WGA signals in the SG lumen. We have now included images from stage 14 and 15 in Figure 5-figure supplement 2C.

Given that luminal Pio signals are lost at stage 16 only and that Dpy signals appear as condensed structures in the lumen of Papss mutants, it suggests that the internalization of luminal proteins is not impaired in Papss mutants. Rather, these proteins are secreted but fail to organize properly.

Line 366. Luminal morphology is characterized by bulging and constrictions. In the trachea, bulges indicate the deformation of the apical membrane and the detachment from the aECM. I can see constrictions and the collapsed tube lumen in Fig. 6C, but I don't find the bulges of the apical membrane in pio and Np mutants. Maybe showing it more clearly and with better quality will be helpful.

Since the bulging phenotype appears to vary from sample to sample, we have revised the description of the phenotype to "constrictions" to more accurately reflect the consistent observations. We quantified the number of constrictions along the entire lumen in pio and Np mutants and included the graph in Figure 6F.

The authors state that Papss controls luminal secretion of Pio and Dumpy, as they observe reduced luminal staining of both in papss mutants. However, the mCh-Pio and Dumpy-YFP are secreted towards the lumen. Does papss overexpression change Pio and Dumpy secretion towards the lumen, and could this be another explanation for the multiple phenotypes?

Thank you for the comment. To clarify, we did not observe reduced luminal staining of Pio and Dpy in Papss mutants, nor did we state that Papss controls luminal secretion of Pio and Dpy. In Papss mutants, Pio luminal signals are absent specifically at stage 16 (Figure 5H), whereas strong luminal Pio signals are present until stage 15 (Figure 5G). For Dpy-YFP, the signals are not reduced but condensed in Papss mutants from stages 14-16 (Figure 5D, H).

It remains unclear whether the apparent loss of Pio signals is due to a loss of Pio protein in the lumen or due to epitope masking resulting from protein aggregation or condensation. As noted in our response to Comment 11 internalization of luminal proteins seems unaffected in Papss mutants; proteins like Pio and Dpy are secreted into the lumen but fail to properly organize. Therefore, we have not tested whether Papss overexpression alters the secretion of Pio or Dpy.

In our original submission, we incorrectly stated that uniform luminal mCh-Pio signals were unchanged in Papss mutants. Upon closer examination, we found these signals are absent in the expanded luminal region in stage 16 SG (where Dpy-YFP is also absent), and weak mCh-Pio signals colocalize with the condensed Dpy-YFP signals (Figure 5C, D). We have revised the text accordingly.

Regulation of luminal ZP protein level is essential to modulate the tube expansion; therefore, Np releases Pio and Dumpy in a controlled manner during st15/16. Thus, the analysis of Pio and Dumpy in NP overexpression embryos will be critical to this manuscript to understand more about the control of luminal ZP matrix proteins.

Thanks for the insightful suggestion. We overexpressed both the WT and mutant form of Np using UAS-Np.WT and UAS-Np.S990A lines (Drees et al., 2019) and analyzed mCh-Pio, Pio antibody, and Dpy-YFP signals. It is important to note that these overexpression experiments were done in the presence of the endogenous WT Np.

Overexpression of Np.WT led to increased levels of mCh-Pio, Pio, and Dpy-YFP signals in the lumen and at the apical membrane. In contrast, overexpression of Np.S990A resulted in a near complete loss of luminal mCh-Pio signals. Pio antibody signals remained strong at the apical membrane but was weaker in the luminal filamentous structures compared to WT.

Due to the GFP tag present in the UAS-Np.S990A line, we could not reliably analyze Dpy-YFP signals because of overlapping fluorescent signals in the same channel. However, the filamentous Pio signals in the lumen co-localized with GFP signals, suggesting that these structures might also include Dpy-YFP, although this cannot be confirmed definitively.

These results suggest that overexpressed Np.S990A may act in a dominant-negative manner, competing with endogenous Np and impairing proper cleavage of Pio (and mCh-Pio). Nevertheless, some level of cleavage by endogenous Np still appears to occur, as indicated by the residual luminal filamentous Pio signals. These new findings have been incorporated into the revised manuscript and are shown in Figure 6H and 6I.

Minor: Fig. 5 C': mChe-Pio and Dumpy-YFP are mixed up at the top of the images.

Thanks for catching this error. It has been corrected.

Sup. Fig7. A shows Pio in purple but B in green. Please indicate it correctly.

It has been corrected.

Reviewer #1 (Significance (Required)):

In 2023, the functions of Pio, Dumpy, and Np in the tracheal tubes of Drosophila were published. The study here shows similar results, with the difference that the salivary glands do not possess chitin, but the two ZP proteins Pio and Dumpy take over its function. It is, therefore, a significant and exciting extension of the known function of the three proteins to another tube system. In addition, the authors identify papss as a new protein and show its essential function in forming the luminal matrix in the salivary glands. Considering the high degree of conservation of these proteins in other species, the results presented are crucial for future analyses and will have further implications for tubular development, including humans.

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

Summary: There is growing appreciation for the important of luminal (apical) ECM in tube development, but such matrices are much less well understood than basal ECMs. Here the authors provide insights into the aECM that shapes the Drosophila salivary gland (SG) tube and the importance of PAPSS-dependent sulfation in its organization and function.

The first part of the paper focuses on careful phenotypic characterization of papss mutants, using multiple markers and TEM. This revealed reduced markers of sulfation (Alcian Blue staining) and defects in both apical and basal ECM organization, Golgi (but not ER) morphology, number and localization of other endosomal compartments, plus increased cell death. The authors focus on the fact that papss mutants have an irregular SG lumen diameter, with both narrowed regions and bulged regions. They address the pleiotropy, showing that preventing the cell death and resultant gaps in the tube did not rescue the SG luminal shape defects and discussing similarities and differences between the papss mutant phenotype and those caused by more general trafficking defects. The analysis uses a papss nonsense mutant from an EMS screen - I appreciate the rigorous approach the authors took to analyze transheterozygotes (as well as homozygotes) plus rescued animals in order to rule out effects of linked mutations.

The 2nd part of the paper focuses on the SG aECM, showing that Dpy and Pio ZP protein fusions localize abnormally in papss mutants and that these ZP mutants (and Np protease mutants) have similar SG lumen shaping defects to the papss mutants. A key conclusion is that SG lumen defects correlate with loss of a Pio+Dpy-dependent filamentous structure in the lumen. These data suggest that ZP protein misregulation could explain this part of the papss phenotype.

Overall, the text is very well written and clear. Figures are clearly labeled. The methods involve rigorous genetic approaches, microscopy, and quantifications/statistics and are documented appropriately. The findings are convincing, with just a few things about the fusions needing clarification.

minor comments 1. Although the Dpy and Qsm fusions are published reagents, it would still be helpful to mention whether the tags are C-terminal as suggested by the nomenclature, and whether Westerns have been performed, since (as discussed for Pio) cleavage could also affect the appearance of these fusions.

Thanks for the comment. Dpy-YFP is a knock-in line in which YFP is inserted into the middle of the dpy locus (Lye et al., 2014; the insertion site is available on Flybase). mCh-Qsm is also a knock-in line, with mCh inserted near the N-terminus of the qsm gene using phi-mediated recombination using the qsmMI07716 line (Chu and Hayashi, 2021; insertion site available on Flybase). Based on this, we have updated the nomenclature from Qsm-mCh to mCh-Qsm throughout the manuscript to accurately reflect the tag position. To our knowledge, no western blot has been performed on Dpy-YFP or mCh-Qsm lines. We have mentioned this explicitly in the Discussion.

The Dpy-YFP reagent is a non-functional fusion and therefore may not be a wholly reliable reporter of Dpy localization. There is no antibody confirmation. As other reagents are not available to my knowledge, this issue can be addressed with text acknowledgement of possible caveats.

Thanks for raising this important point. We have added a caveat in the Discussion noting this limitation and the need for additional tools, such as an antibody or a functional fusion protein, to confirm the localization of Dpy.

TEM was done by standard chemical fixation, which is fine for viewing intracellular organelles, but high pressure freezing probably would do a better job of preserving aECM structure, which looks fairly bad in Fig. 2G WT, without evidence of the filamentous structures seen by light microscopy. Nevertheless, the images are sufficient for showing the extreme disorganization of aECM in papss mutants.

We agree that HPF is a better method and intent to use the HPF system in future studies. We acknowledge that chemical fixation contributes to the appearance of a gap between the apical membrane and the aECM, which we did not observe in the HPF/FS method (Chung and Andrew, 2014). Despite this, the TEM images still clearly reveal that Papss mutants show a much thinner and more electron-dense aECM compared to WT (Figure 2H, I), consistent to the condensed WGA, Dpy, and Pio signals in our confocal analyses. As the reviewer mentioned, we believe that the current TEM data are sufficient to support the conclusion of severe aECM disorganization and Golgi defects in Papss mutants.

The authors may consider citing some of the work that has been done on sulfation in nematodes, e.g. as reviewed here: https://pubmed.ncbi.nlm.nih.gov/35223994/ Sulfation has been tied to multiple aspects of nematode aECM organization, though not specifically to ZP proteins.

Thank you for the suggestion. Pioneering studies in C. elegans have highlighted the key role of sulfation in diverse developmental processes, including neuronal organization, reproductive tissue development, and phenotypic plasticity. We have now cited several works.

Reviewer #2 (Significance (Required)):

This study will be of interest to researchers studying developmental morphogenesis in general and specifically tube biology or the aECM. It should be particularly of interest to those studying sulfation or ZP proteins (which are broadly present in aECMs across organisms, including humans).

This study adds to the literature demonstrating the importance of luminal matrix in shaping tubular organs and greatly advances understanding of the luminal matrix in the Drosophila salivary gland, an important model of tubular organ development and one that has key matrix differences (such as no chitin) compared to other highly studied Drosophila tubes like the trachea.

The detailed description of the defects resulting from papss loss suggests that there are multiple different sulfated targets, with a subset specifically relevant to aECM biology. A limitation is that specific sulfated substrates are not identified here (e.g. are these the ZP proteins themselves or other matrix glycoproteins or lipids?); therefore it's not clear how direct or indirect the effects of papss are on ZP proteins. However, this is clearly a direction for future work and does not detract from the excellent beginning made here.

My expertise: I am a developmental geneticist with interests in apical ECM

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

In this work Woodward et al focus on the apical extracellular matrix (aECM) in the tubular salivary gland (SG) of Drosophila. They provide new insights into the composition of this aECM, formed by ZP proteins, in particular Pio and Dumpy. They also describe the functional requirements of PAPSS, a critical enzyme involved in sulfation, in regulating the expansion of the lumen of the SG. A detailed cellular analysis of Papss mutants indicate defects in the apical membrane, the aECM and in Golgi organization. They also find that Papss control the proper organization of the Pio-Dpy matrix in the lumen. The work is well presented and the results are consistent.

Main comments

• This work provides a detailed description of the defects produced by the absence of Papss. In addition, it provides many interesting observations at the cellular and tissular level. However, this work lacks a clear connection between these observations and the role of sulfation. Thus, the mechanisms underlying the phenotypes observed are elusive. Efforts directed to strengthen this connection (ideally experimentally) would greatly increase the interest and relevance of this work.

Thank you for this thoughtful comment. To directly test whether the phenotypes observed in Papss mutants are due to the loss of sulfation activity, we generated transgenic lines expressing catalytically inactive forms of Papss, UAS-PapssK193A, F593P, in which key residues in the APS kinase and ATP sulfurylase domains are mutated. Unlike WT UAS-Papss (both the Papss-PD or Papss-PE isoforms), the catalytically inactive UAS-Papssmut failed to rescue any of the phenotypes, including the thin lumen phenotype (Figure 1I-L), altered WGA signals (Figure I, I') and the cell death phenotype (Figure 4D, E). These findings strongly support the conclusion that the enzymatic sulfation activity of Papss is essential for the developmental processes described in this study.

• A main issue that arises from this work is the role of Papss at the cellular level. The results presented convincingly indicate defects in Golgi organization in Papss mutants. Therefore, the defects observed could stem from general defects in the secretion pathway rather than from specific defects on sulfation. This could even underly general/catastrophic cellular defects and lead to cell death (as observed). This observation has different implications. Is this effect observed in SGs also observed in other cells in the embryo? If Papss has a general role in Golgi organization this would be expected, as Papss encodes the only PAPs synthatase in Drosophila. Can the authors test any other mutant that specifically affect Golgi organization and investigate whether this produces a similar phenotype to that of Papss?

Thank you for the comment. To address whether the defects observed in Papss mutants stem from general disruption of the secretory pathway due to Golgi disorganization, we examined mutants of two key Golgi components: Grasp65 and GM130.

In Grasp65 mutants, we observed significant defects in SG lumen morpholgy, including highly irregular SG lumen shape and multiple constrictions (100%; n=10/10). However, the lumen was not uniformly thin as in Papss mutants. In contrast, GM130 mutants-although this line was very sick and difficult to grow-showed relatively normal salivary glands morphology in the few embryos that survived to stage 16 (n=5/5). It is possible that only embryos with mild phenotypes progressed to this stages, limiting interpretation. These data have now been included in Figure 3-figure supplement 2. Overall, while Golgi disruption can affect SG morphology, the specific phenotypes seen in Papss mutants are not fully recapitulated by Grasp65 or GM130 loss.

• A model that conveys the different observations and that proposes a function for Papss in sulfation and Golgi organization (independent or interdependent?) would help to better present the proposed conclusions. In particular, the paper would be more informative if it proposed a mechanism or hypothesis of how sulfation affects SG lumen expansion. Is sulfation regulating a factor that in turn regulates Pio-Dpy matrix? Is it regulating Pio-Dpy directly? Is it regulating a product recognized by WGA? For instance, investigating Alcian blue or sulfotyrosine staining in pio, dpy mutants could help to understand whether Pio, Dpy are targets of sulfation.

Thank you for the comment. We're also very interested in learning whether the regulation of the Pio-Dpy matrix is a direct or indirect consequence of the loss of sulfation on these proteins. One possible scenario is that sulfation directly regulates the Pio-Dpy matrix by regulating protein stability through the formation of disulfide bonds between the conserved Cys residues responsible for ZP module polymerization. Additionally, the Dpy protein contains hundreds of EGF modules that are highly susceptible to O-glycosylation. Sulfation of the glycan groups attached to Dpy may be critical for its ability to form a filamentous structure. Without sulfation, the glycan groups on Dpy may not interact properly with the surrounding materials in the lumen, resulting in an aggregated and condensed structure. These possibilities are discussed in the Discussion.

We have not analyzed sulfation levels in pio or dpy mutants because sulfation levels in mutants of single ZP domain proteins may not provide much information. A substantial number of proteoglycans, glycoproteins, and proteins (with up to 1% of all tyrosine residues in an organism's proteins estimated to be sulfated) are modified by sulfation, so changes in sulfation levels in a single mutant may be subtle. Especially, the existing dpy mutant line is an insertion mutant of a transposable element; therefore, the sulfation sites would still remain in this mutant.

• Interpretation of Papss effects on Pio and Dpy would be desired. The results presented indicate loss of Pio antibody staining but normal presence of cherry-Pio. This is difficult to interpret. How are these results of Pio antibody and cherry-Pio correlating with the results in the trachea described recently (Drees et al. 2023)?

In our original submission, we stated that the uniform luminal mCh-Pio signals were not changed in Papss mutants, but after re-analysis, we found that these signals were actually absent from the expanded luminal region in stage 16 SG (where Dpy-YFP is also absent), and weak mCh-Pio signals colocalize with the condensed Dpy-YFP signals (Figure 5C, D). We have revised the text accordingly.

After cleavages by Np and furin, the Pio protein should have three fragments. The N-terminal region contains the N-terminal half of the ZP domain, and mCh-Pio signals show this fragment. The very C-terminal region should localize to the membrane as it contains the transmembrane domain. We think the middle piece, the C-terminal ZP domain, is recognized by the Pio antibody. The mCh-Pio and Pio antibody signals in the WT trachea (Drees et al., 2023) are similar to those in the SG. mCh-Pio signals are detected in the tracheal lumen as uniform signals, at the apical membrane, and in cytoplasmic puncta. Pio antibody signals are exclusively in the tracheal lumen and show more heterogenous filamentous signals.

In Papss mutants, the middle fragment (the C-terminal ZP domain) seems to be most affected because the Pio antibody signals are absent from the lumen. The loss of Pio antibody signals could be due to protein degradation or epitope masking caused by aECM condensation and protein misfolding. This fragment seems to be key for interacting with Dpy, since Pio antibody signals always colocalize with Dpy-YFP. The N-terminal mCh-Pio fragment does not appear to play a significant role in forming a complex with Dpy in WT (but still aggregated together in Papss mutants), and this can be tested in future studies.

In response to Reviewer 1's comment, we performed an additional experiment to test the role of Np in cleaving Pio to help organize the SG aECM. In this experiment, we overexpressed the WT and mutant form of Np using UAS-Np.WT and UAS-Np.S990A lines (Drees et al., 2019) and analyzed mCh-Pio, Pio antibody, and Dpy-YFP signals. Np.WT overexpression resulted in increased levels of mCh-Pio, Pio, and Dpy-YFP signals in the lumen and at the apical membrane. However, overexpression of Np.S990A resulted in the absence of luminal mCh-Pio signals. Pio antibody signals were strong at the apical membrane but rather weak in the luminal filamentous structures. Since the UAS-Np.S990A line has the GFP tag, we could not reliably analyze Dpy-YFP signals due to overlapping Np.S990A.GFP signals in the same channel. However, the luminal filamentous Pio signals co-localized with GFP signals, and we assume that these overlapping signals could be Dpy-YFP signals.

These results suggest that overexpressed Np.S990A may act in a dominant-negative manner, competing with endogenous Np and impairing proper cleavage of Pio (and mCh-Pio). Nevertheless, some level of cleavage by endogenous Np still appears to occur, as indicated by the residual luminal filamentous Pio signals. These new findings have been incorporated into the revised manuscript and are shown in Figure 6H and 6I.

A proposed model of the Pio-Dpy aECM in WT, Papss, pio, and Np mutants has now been included in Figure 7.

• What does the WGA staining in the lumen reveal? This staining seems to be affected differently in pio and dpy mutants: in pio mutants it disappears from the lumen (as dpy-YFP does), but in dpy mutants it seems to be maintained. How do the authors interpret these findings? How does the WGA matrix relate to sulfated products (using Alcian blue or sulfotyrosine)?

WGA binds to sialic acid and N-acetylglucosamine (GlcNAc) residues on glycoproteins and glycolipids. GlcNAc is a key component of the glycosaminoglycan (GAG) chains that are covalently attached to the core protein of a proteoglycan, which is abundant in the ECM. We think WGA detects GlcNAc residues in the components of the aECM, including Dpy as a core component, based on the following data. 1) WGA and Dpy colocalize in the lumen, both in WT (as thin filamentous structures) and Papss mutant background (as condensed rod-like structures), and 2) are absent in pio mutants. WGA signals are still present in a highly condensed form in dpy mutants. That's probably because the dpy mutant allele (dpyov1) has an insertion of a transposable element (blood element) into intron 11 and this insertion may have caused the Dpy protein to misfold and condense. We added the information about the dpy allele to the Results section and discussed it in the Discussion.

Minor points:

• The morphological phenotypic analysis of Papss mutants (homozygous and transheterozygous) is a bit confusing. The general defects are higher in Papss homozygous than in transheterozygotes over a deficiency. Maybe quantifying the defects in the heterozygote embryos in the Papss mutant collection could help to figure out whether these defects relate to Papss mutation.

We analyzed the morphology of heterozygous Papss mutant embryos. They were all normal. The data and quantifications have now been added to Figure 1-figure supplement 3.

• The conclusion that the apical membrane is affected in Papss mutants is not strongly supported by the results presented with the pattern of Crb (Fig 2). Further evidences should be provided. Maybe the TEM analysis could help to support this conclusion

We quantified Crb levels in the sub-apical and medial regions of the cell and included this new quantification in Figure 2D. TEM images showed variation in the irregularity of the apical membrane, even in WT, and we could not draw a solid conclusion from these images.

• It is difficult to understand why in Papss mutants the levels of WGA increase. Can the authors elaborate on this?

We think that when Dpy (and many other aECM components) are condensed and aggregated into the thin, rod-like structure in Papss mutants, the sugar residues attached to them must also be concentrated and shown as increased WGA signals.

• The explanation about why Pio antibody and mcherry-Pio show different patterns is not clear. If the antibody recognizes the C-t region, shouldn't it be clearly found at the membrane rather than the lumen?

The Pio protein is also cleaved by furin protease (Figure 5B). We think the Pio fragment recognized by the antibody should be a "C-terminal ZP domain", which is a middle piece after furin + Np cleavages.

• The qsm information does not seem to provide any relevant information to the aECM, or sulfation.

Since Qsm has been shown to bind to Dpy and remodel Dpy filaments in the muscle tendon (Chu and Hayashi, 2021), we believe that the different behavior of Qsm in the SG is still informative. As mentioned briefly in the Discussion, the cleaved Qsm fragment may localize differently, like Pio, and future work will need to test this. We have shortened the description of the Qsm localization in the manuscript and moved the details to the figure legend of Figure 5-figure supplement 3.

Reviewer #3 (Significance (Required)):

Previous reports already indicated a role for Papss in sulfation in SG (Zhu et al 2005). Now this work provides a more detailed description of the defects produced by the absence of Papss. In addition, it provides relevant data related to the nature and requirements of the aECM in the SG. Understanding the composition and requirements of aECM during organ formation is an important question. Therefore, this work may be relevant in the fields of cell biology and morphogenesis.

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Referee #3

Evidence, reproducibility and clarity

In this work Woodward et al focus on the apical extracellular matrix (aECM) in the tubular salivary gland (SG) of Drosophila. They provide new insights into the composition of this aECM, formed by ZP proteins, in particular Pio and Dumpy. They also describe the functional requirements of PAPSS, a critical enzyme involved in sulfation, in regulating the expansion of the lumen of the SG. A detailed cellular analysis of Papss mutants indicate defects in the apical membrane, the aECM and in Golgi organization. They also find that Papss control the proper organization of the Pio-Dpy matrix in the lumen. The work is well presented and the results are consistent.

Main comments:

• This work provides a detailed description of the defects produced by the absence of Papss. In addition, it provides many interesting observations at the cellular and tissular level. However, this work lacks a clear connection between these observations and the role of sulfation. Thus, the mechanisms underlying the phenotypes observed are elusive. Efforts directed to strengthen this connection (ideally experimentally) would greatly increase the interest and relevance of this work.

• A main issue that arises from this work is the role of Papss at the cellular level. The results presented convincingly indicate defects in Golgi organization in Papss mutants. Therefore, the defects observed could stem from general defects in the secretion pathway rather than from specific defects on sulfation. This could even underly general/catastrophic cellular defects and lead to cell death (as observed). This observation has different implications. Is this effect observed in SGs also observed in other cells in the embryo? If Papss has a general role in Golgi organization this would be expected, as Papss encodes the only PAPs synthatase in Drosophila. Can the authors test any other mutant that specifically affect Golgi organization and investigate whether this produces a similar phenotype to that of Papss?

• A model that conveys the different observations and that proposes a function for Papss in sulfation and Golgi organization (independent or interdependent?) would help to better present the proposed conclusions. In particular, the paper would be more informative if it proposed a mechanism or hypothesis of how sulfation affects SG lumen expansion. Is sulfation regulating a factor that in turn regulates Pio-Dpy matrix? Is it regulating Pio-Dpy directly? Is it regulating a product recognized by WGA?<br /> For instance, investigating Alcian blue or sulfotyrosine staining in pio, dpy mutants could help to understand whether Pio, Dpy are targets of sulfation.

• Interpretation of Papss effects on Pio and Dpy would be desired. The results presented indicate loss of Pio antibody staining but normal presence of cherry-Pio. This is difficult to interpret. How are these results of Pio antibody and cherry-Pio correlating with the results in the trachea described recently (Drees et al. 2023)?

• What does the WGA staining in the lumen reveal? This staining seems to be affected differently in pio and dpy mutants: in pio mutants it disappears from the lumen (as dpy-YFP does), but in dpy mutants it seems to be maintained. How do the authors interpret these findings? How does the WGA matrix relate to sulfated products (using Alcian blue or sulfotyrosine)?.

Minor points:

• The morphological phenotypic analysis of Papss mutants (homozygous and transheterozygous) is a bit confusing. The general defects are higher in Papss homozygous than in transheterozygotes over a deficiency. Maybe quantifying the defects in the heterozygote embryos in the Papss mutant collection could help to figure out whether these defects relate to Papss mutation.

• The conclusion that the apical membrane is affected in Papss mutants is not strongly supported by the results presented with the pattern of Crb (Fig 2). Further evidences should be provided. Maybe the TEM analysis could help to support this conclusion

• It is difficult to understand why in Papss mutants the levels of WGA increase. Can the authors elaborate on this?

• The explanation about why Pio antibody and mcherry-Pio show different patterns is not clear. If the antibody recognizes the C-t region, shouldn't it be clearly found at the membrane rather than the lumen?

• The qsm information does not seem to provide any relevant information to the aECM, or sulfation.

Significance

Previous reports already indicated a role for Papss in sulfation in SG (Zhu et al 2005). Now this work provides a more detailed description of the defects produced by the absence of Papss. In addition, it provides relevant data related to the nature and requirements of the aECM in the SG. Understanding the composition and requirements of aECM during organ formation is an important question. Therefore, this work may be relevant in the fields of cell biology and morphogenesis.

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Referee #2

Evidence, reproducibility and clarity

Summary:

There is growing appreciation for the important of luminal (apical) ECM in tube development, but such matrices are much less well understood than basal ECMs. Here the authors provide insights into the aECM that shapes the Drosophila salivary gland (SG) tube and the importance of PAPSS-dependent sulfation in its organization and function.

The first part of the paper focuses on careful phenotypic characterization of papss mutants, using multiple markers and TEM. This revealed reduced markers of sulfation (Alcian Blue staining) and defects in both apical and basal ECM organization, Golgi (but not ER) morphology, number and localization of other endosomal compartments, plus increased cell death. The authors focus on the fact that papss mutants have an irregular SG lumen diameter, with both narrowed regions and bulged regions. They address the pleiotropy, showing that preventing the cell death and resultant gaps in the tube did not rescue the SG luminal shape defects and discussing similarities and differences between the papss mutant phenotype and those caused by more general trafficking defects. The analysis uses a papss nonsense mutant from an EMS screen - I appreciate the rigorous approach the authors took to analyze transheterozygotes (as well as homozygotes) plus rescued animals in order to rule out effects of linked mutations.

The 2nd part of the paper focuses on the SG aECM, showing that Dpy and Pio ZP protein fusions localize abnormally in papss mutants and that these ZP mutants (and Np protease mutants) have similar SG lumen shaping defects to the papss mutants. A key conclusion is that SG lumen defects correlate with loss of a Pio+Dpy-dependent filamentous structure in the lumen. These data suggest that ZP protein misregulation could explain this part of the papss phenotype.

Overall, the text is very well written and clear. Figures are clearly labeled. The methods involve rigorous genetic approaches, microscopy, and quantifications/statistics and are documented appropriately. The findings are convincing, with just a few things about the fusions needing clarification.

Minor comments:

1. Although the Dpy and Qsm fusions are published reagents, it would still be helpful to mention whether the tags are C-terminal as suggested by the nomenclature, and whether Westerns have been performed, since (as discussed for Pio) cleavage could also affect the appearance of these fusions.

2. The Dpy-YFP reagent is a non-functional fusion and therefore may not be a wholly reliable reporter of Dpy localization. There is no antibody confirmation. As other reagents are not available to my knowledge, this issue can be addressed with text acknowledgement of possible caveats.

3. TEM was done by standard chemical fixation, which is fine for viewing intracellular organelles, but high pressure freezing probably would do a better job of preserving aECM structure, which looks fairly bad in Fig. 2G WT, without evidence of the filamentous structures seen by light microscopy. Nevertheless, the images are sufficient for showing the extreme disorganization of aECM in papss mutants.

4. The authors may consider citing some of the work that has been done on sulfation in nematodes, e.g. as reviewed here: https://pubmed.ncbi.nlm.nih.gov/35223994/ Sulfation has been tied to multiple aspects of nematode aECM organization, though not specifically to ZP proteins.

Significance

This study will be of interest to researchers studying developmental morphogenesis in general and specifically tube biology or the aECM. It should be particularly of interest to those studying sulfation or ZP proteins (which are broadly present in aECMs across organisms, including humans).

This study adds to the literature demonstrating the importance of luminal matrix in shaping tubular organs and greatly advances understanding of the luminal matrix in the Drosophila salivary gland, an important model of tubular organ development and one that has key matrix differences (such as no chitin) compared to other highly studied Drosophila tubes like the trachea.

The detailed description of the defects resulting from papss loss suggests that there are multiple different sulfated targets, with a subset specifically relevant to aECM biology. A limitation is that specific sulfated substrates are not identified here (e.g. are these the ZP proteins themselves or other matrix glycoproteins or lipids?); therefore it's not clear how direct or indirect the effects of papss are on ZP proteins. However, this is clearly a direction for future work and does not detract from the excellent beginning made here.

My expertise: I am a developmental geneticist with interests in apical ECM

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Referee #1

Evidence, reproducibility and clarity

PAPS is required for all sulfotransferase reactions in which a sulfate group is covalently attached to amino acid residues of proteins or to side chains of proteoglycans. This sulfation is crucial for properly organizing the apical extracellular matrix (aECM) and expanding the lumen in the Drosophila salivary gland. Loss of Papss potentially leads to decreased sulfation, disorganizing the aECM, and defects in lumen formation. In addition, Papss loss destabilizes the Golgi structures.

In Papss mutants, several changes occur in the salivary gland lumen of Drosophila. The tube lumen is very thin and shows irregular apical protrusions. There is a disorganization of the apical membrane and a compaction of the apical extracellular matrix (aECM). The Golgi structures and intracellular transport are disturbed. In addition, the ZP domain proteins Piopio (Pio) and Dumpy (Dpy) lose their normal distribution in the lumen, which leads to condensation and dissociation of the Dpy-positive aECM structure from the apical membrane. This results in a thin and irregularly dilated lumen.

1. The authors describe various changes in the lumen in mutants, from thin lumen to irregular expansion. I would like to know the correct lumen diameter, and length, besides the total area, by which one can recognize thin and irregular.

2. The rescue is about 30%, which is not as good as expected. Maybe the wrong isoform was taken. Is it possible to find out which isoform is expressed in the salivary glands, e.g., by RNA in situ Hyb? This could then be used to analyze a more focused rescue beyond the paper.

3. Crb is a transmembrane protein on the apicolateral side of the membrane. Accordingly, the apicolateral distribution can be seen in the control and the mutant. I believe there are no apparent differences here, not even in the amount of expression. However, the view of the cells (frame) shows possible differences. To be sure, a more in-depth analysis of the images is required. Confocal Z-stack images, with 3D visualization and orthogonal projections to analyze the membranes showing Crb staining together with a suitable membrane marker (e.g. SAS or Uif). This is the only way to show whether Crb is incorrectly distributed. Statistics of several papas mutants would also be desirable and not just a single representative image. When do the observed changes in Crb distribution occur in the development of the tubes, only during stage 16? Is papass only involved in the maintenance of the apical membrane? This is particularly important when considering the SJ and AJ, because the latter show no change in the mutants.

4. A change in the ECM is only inferred based on the WGA localization. This is too few to make a clear statement. WGA is only an indirect marker of the cell surface and glycosylated proteins, but it does not indicate whether the ECM is altered in its composition and expression. Other important factors are missing here. In addition, only a single observation is shown, and statistics are missing.

5. Reduced WGA staining is seen in papas mutants, but this could be due to other circumstances. To be sure, a statistic with the number of dots must be shown, as well as an intensity blot on several independent samples. The images are from single confocal sections. It could be that the dots appear in a different Z-plane. Therefore, a 3D visualization of the voxels must be shown to identify and, at best, quantify the dots in the organ.

6. A colocalization analysis (statistics) should be shown for the overlap of WGA with ManII-GFP.

7. I do not understand how the authors describe "statistics of secretory vesicles" as an axis in Figure 3p. The TEM images do not show labeled secretory vesicles but empty structures that could be vesicles.

8. The quality of the presented TEM images is too low to judge any difference between control and mutants. Therefore, the supplement must present them in better detail (higher pixel number?).

9. Line 266: the conclusion that apical trafficking is "significantly impaired" does not hold. This implies that Papass is essential for apical trafficking, but the analyzed ECM proteins (Pio, Dumpy) are found apically enriched in the mutants, and Dumpy is even secreted. Moreover, they analyze only one marker, Sec15, and don't provide data about the quantification of the secretion of proteins.

10. DCP-1 was used to detect apoptosis in the glands to analyze acellular regions. However, the authors compare ST16 control with ST15 mutant salivary glands, which is problematic. Further, it is not commented on how many embryos were analyzed and how often they detect the dying cells in control and mutant embryos. This part must be improved.

11. WGA and Dumpy show similar condensed patterns within the tube lumen. The authors show that dumpy is enriched from stage 14 onwards. How is it with WGA? Does it show the same pattern from stage 14 to 16? Papass mutants can suffer from a developmental delay in organizing the ECM or lack of internalization of luminal proteins during/after tube expansion, which is the case in the trachea.

12. Line 366. Luminal morphology is characterized by bulging and constrictions. In the trachea, bulges indicate the deformation of the apical membrane and the detachment from the aECM. I can see constrictions and the collapsed tube lumen in Fig. 6C, but I don't find the bulges of the apical membrane in pio and Np mutants. Maybe showing it more clearly and with better quality will be helpful.

13. The authors state that Papass controls luminal secretion of Pio and Dumpy, as they observe reduced luminal staining of both in papass mutants. However, the mCh-Pio and Dumpy-YFP are secreted towards the lumen. Does papass overexpression change Pio and Dumpy secretion towards the lumen, and could this be another explanation for the multiple phenotypes? Regulation of luminal ZP protein level is essential to modulate the tube expansion; therefore, Np releases Pio and Dumpy in a controlled manner during st15/16. Thus, the analysis of Pio and Dumpy in NP overexpression embryos will be critical to this manuscript to understand more about the control of luminal ZP matrix proteins.

14. Minor: Fig. 5 C': mChe-Pio and Dumpy-YFP are mixed up at the top of the images. Sup. Fig7. A shows Pio in purple but B in green. Please indicate it correctly.

Significance

In 2023, the functions of Pio, Dumpy, and Np in the tracheal tubes of Drosophila were published. The study here shows similar results, with the difference that the salivary glands do not possess chitin, but the two ZP proteins Pio and Dumpy take over its function. It is, therefore, a significant and exciting extension of the known function of the three proteins to another tube system. In addition, the authors identify papass as a new protein and show its essential function in forming the luminal matrix in the salivary glands. Considering the high degree of conservation of these proteins in other species, the results presented are crucial for future analyses and will have further implications for tubular development, including humans.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

This study characterizes autoimmunity in mutant lines of Arabidopsis that are lacking components of the m6A methyltransferase complex (MTC). The molecular results and bacterial pathogen resistance of the lines at low temps as compared to high temps support this hypothesis. However, the phenotypic analysis or new complete lack there of (Figure 6), makes the hypothesis and overall story much less convincing. I give some comments for improving the figures below.

Figure 6 showing the phenotypes in its current set up is very uninformative. More informative pictures and quantitative analyses of specific developmental phenotypes should be added to show the differences between the phenotypes of the mutant and wild-type plants at the two different temperatures. As of now the reader gets a sense of nothing from the figure. Without this Figure demonstrating a major rescue of phenotype at the 27C temperature the reader is not convinced that the autoimmunity is the major cause of the phenotype

Supplemental Figure 1 is missing from the review file.

Significance

It is notable that a couple of recent studies have already shown the increased resistance of MTC component mutants to pathogens (Prall et al. 2024 and Chen et al. 2024), which weakens the impact of the overall findings. In my honest assessment, this study would be well positioned for publication in a mid-tier plant specific journal (e.g. Plant Physiology) based on the currently included results.

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Metheringham et al. reports on interesting new characterizations of phenotypes caused by genetic inactivation of subunits of the methyl transferase complex responsible for N6-adenosine methylation in (pre)-mRNA ("the m6A writer") in the plant Arabidopsis thaliana. The main claim of the paper is that mutants in these subunits exhibit autoimmunity, a claim that is supported by the following lines of evidence:

• Transcriptome profiling by mRNA-seq shows a gene expression profile with differential expression of many stress- and defense-related genes.
• The immunity-like gene expression profile is observed under growth at 17{degree sign}C but not at 27{degree sign}C, consistent with the well-known temperature-sensitivity of some (but not all) innate immunity signaling systems in plants.
• m6A writer mutants show increased resistance to infection by the virulent Pseudomonas syringae DC3000 strain.
• The primary biochemical defect in m6A writing is not temperature sensitive, excluding the trivial possibility that the mutant alleles chosen for study are simply ts.

The observations are important and the manuscript is very well written, a pleasure to read: the problem is clearly presented, the experimental results are presented in a clear, logical succession, and the discussion treats important points.

The study is valuable pending some manuscript revision on the autoimmunity interpretation of the results obtained, and a few suggested edits that can be included if the authors agree that they would improve the paper.

The finding that an autoimmune-like state is activated in m6A writer mutants is significant because it provides a warning flag on how such mutants should be used for studying the role of m6A in stress response signaling, including reassessment of previously published work. Whether the stress state really is autoimmunity is subject to some debate, particularly because no genetic evidence to support it has been obtained. The results are nonetheless interesting and constitute an important contribution to the community, even if they remain descriptive and with nearly no insight into molecular mechanisms. My suggestions for improvement are summarized below.

1. Although the authors do a lot to support the claim that autoimmunity is an element of m6A writer mutant phenotypes, the study does not include genetic evidence to support this claim. This is important, because if the stress/defense gene activation causes some of the morphological phenotypes of m6A writer mutants, one should be able to suppress such defects by mutation of know immune signaling components such as the appropriate nucleotide-binding leucine-rich repeat proteins, or more generic signaling components such as EDS1, PAD4 and SAG1, common to a subset of such intracellular immune receptors. Resistance to pathogens can be observed in mutants with constitutive stress response signaling, and defense-like gene expression can be induced as a secondary of other primary defects, for instance DNA damage. Similarly, while it is true that some types of immune activation are temperature sensitive, others are not 1, and clearly, elevated temperature changes so much of the physiology of the plant that sensitivity to elevated temperature cannot be used as proof of immune activation. Thus, each of the lines of evidence presented is suggestive, not conclusive. Together, they constitute a good argument, but still not a completely satisfactory proof of the main claim. I do not think that this concern means that a lot of genetic work must be undertaken to make this paper publishable, but I think that the authors should be even more careful about how they interpret their observations. I understand that they favor more or less direct activation of autoimmunity, although even if that were true, it would be unclear what the biochemical triggers of such autoimmunity would be (unmethylated RNA, absence or writer components, excess of free m6A-binding proteins etc). However, given the concerns above, I think the authors should dedicate a small paragraph in the discussion to the possibility that the primary cause of stress/defense-gene expression is unclear and may not result from innate immune surveillance of unmethylated mRNA or components of the m6A pathway as favoured by the authors.
2. It may be of relevance to search promoters of differentially expressed genes for enrichment of cis-elements. This simple approach identified the W-box in the first papers using transcriptome profiling to characterize the immune state in Arabidopsis 2,3, and could perhaps reveal whether a WRKY-driven transcriptional program drives differential expression or whether several other transcription factor classes may also contribute substantially, as may be expected if a more complex stress-related transcriptional program is activated. I do not think that this is a deal breaker, but some additional useful information from the existing data might be gathered in this way.
3. Stress response activation has also been clearly described in ect2 ect3 ect4 mutants4 and even if the authors find no evidence for PR1 expression in this mutant, it is still of relevance to include a mention of this result in the discussion, together with the discussion of stress response activation seen in writer mutants in earlier reports 5,6. I would not mind the authors being a bit more explicit about what their results mean for studies that try to conclude on the biological relevance of m6A in different types of stress signaling, using phenotypes writer mutants as their primary line of evidence. But this is of course up to the authors to decide on that.
4. In the introduction on preferred m6A sequence contexts, please clarify that m6A in plants occurs both DRACH in (G)GAU contexts 7,8.
5. When mentioning convergence on shared signaling components from immune receptors, please include a tiny bit more information for the reader. For instance, EDS1 is mentioned, but this protein is only required for signaling from (some) TIR-NBS-LRRs, not the class of CC-NBS-LRRs. Indeed, signaling by this latter class may not converge on just one to a few components, as their multimerization appears to form the ion channels required for signaling-inducing ion currents.
6. Please clarify in the introduction and in later parts that only some forms of autoimmunity can be suppressed by elevated temperature. Sentences like "A hallmark of Arabidopsis autoimmunity is temperature sensitivity..." are a bit misleading. Temperature sensitivity has clearly been used to study some forms of EDS1-dependent immunity, to great effect in the TMV-N interaction for instance, but it is not accurate to call temperature sensitivity a "hallmark of autoimmunity".
7. In the discussion of possible biochemical triggers of autoimmunity in m6A mutants, please consider the following:

(A) Mention the possibility that the primary trigger may not be immune receptor-surveillance of some defect induced by lack of m6A in mRNA (as discussed above).

(B) In connection with the consideration that lack of m6A writer components, not m6A in mRNA, may be a signal, you could include the observation from yeast that Ime4 knockouts have a much stronger phenotype than Ime4 catalytically dead mutants or knockouts of the sole yeast YTH-domain Pho92 9. Indeed, it is a bit of an embarrassment to the plant m6A community that we have not yet examined phenotypes of MTA and MTB catalytically dead mutants, and the present report should further urge the community to finally do this important experiment. 8. Just a tiny typo on page 15, Pst DC3000, not Pst D3000 (of no relevance to the overall assessment, just a help to eliminate annoying errors before final submission).

REFERENCES

1. Demont, H. et al. Downstream signaling induced by several plant Toll/interleukin-1 receptor-containing immune proteins is stable at elevated temperature. Cell Reports 44(2025).
2. Petersen, M. et al. Arabidopsis MAP kinase 4 negatively regulates systemic acquired resistance. Cell 103, 1111-1120 (2000).
3. Maleck, K. et al. The transcriptome of Arabidopsis thaliana during systemic acquired resistance. Nature Genetics 26, 403-410 (2000).
4. Arribas-Hernández, L. et al. The YTHDF proteins ECT2 and ECT3 bind largely overlapping target sets and influence target mRNA abundance, not alternative polyadenylation. eLife 10, e72377 (2021).
5. Bodi, Z. et al. Adenosine Methylation in Arabidopsis mRNA is Associated with the 3' End and Reduced Levels Cause Developmental Defects. Front Plant Sci 3, 48 (2012).
6. Prall, W. et al. Pathogen-induced m6A dynamics affect plant immunity. The Plant Cell 35, 4155-4172 (2023).
7. Arribas-Hernández, L. et al. Principles of mRNA targeting via the Arabidopsis m6A-binding protein ECT2. eLife 10, e72375 (2021).
8. Wang, G. et al. Quantitative profiling of m6A at single base resolution across the life cycle of rice and Arabidopsis. Nature Communications 15, 4881 (2024).
9. Ensinck, I. et al. The yeast RNA methylation complex consists of conserved yet reconfigured components with m6A-dependent and independent roles. eLife 12, RP87860 (2023).

Significance

The finding that an autoimmune-like state is activated in m6A writer mutants is significant because it provides a warning flag on how such mutants should be used for studying the role of m6A in stress response signaling, including reassessment of previously published work. Whether the stress state really is autoimmunity is subject to some debate, particularly because no genetic evidence to support it has been obtained. The results are nonetheless interesting and constitute an important contribution to the community, even if they remain descriptive and with nearly no insight into molecular mechanisms. I wish to congratulate the authors on another valuable contribution to the plant m6A field.

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors aim to understand the consequences of disrupting N6 methyladenosine, an abundant mRNA modification in plants and other organisms, in Arabidopsis. Genetic ablation of the N6 methyladenosine transferase complex is embryonic lethal in Arabidopsis. Therefore, the authors utilize a hypomorphic allele of VIRILIZER, a component of the complex, to examine gene expression changes and other phenotypes. The authors demonstrate that immune response pathway genes are misregulated in the vir mutant. This transcriptional phenotype is suppressed at higher temperatures, although developmental phenotypes are not. The manuscript provides strong evidence that reduced function of the m6A methyltransferase complex leads to upregulation of immune response genes, although a mechanistic connection between the immune response and m6A in mRNA is not discerned.

Major comments

The major claims of the manuscript are that disrupting the m6A writer complex triggers an autoimmune response that is present at 17C and suppressed at 27C (in line with known aspects of Arabidopsis immunity). Consistent with this, they also show that at 17C the vir-1 mutant has more cell death and is more resistant to infection by Pseudomonas syringae. All of these claims are well supported by the data. The authors also claim that polyA tail lengths are different between the two temperatures. They further speculate that mRNAs that lack m6A trigger immune signaling, but this is not directly tested in the study.

The conclusions about transcriptional activation of the immune response at lower temperatures are sufficiently supported by two types of mRNA sequencing data (direct RNA sequencing and short-read sequences) and appropriate biological replication. The initial profiling was at 22 C, later profiling was at 17C and 27 C. How similar/overlapping were the vir-1 misregulated genes at 17C and 22C? Is the immune response transcriptional signature stronger at 17C than at 22C? The authors sought to determine whether the vir-1 response at 17C was due to pathogen infection of those plants. They used their Illumina RNA-seq data to try and identify pathogen RNAs. They report that there was no significant enrichment of plant pathogen sequences (supplemental table 7). Significant compared to what? Supplemental Table 7 does not indicate that the WT data was assessed and there's no information on significance of enrichment (or nothing obvious, based on column titles). Did the Illumina library prep preparation rely on polyA tails? If so, this is not a sensitive assay to detect bacterial transcripts.

I found the last section on altered poly(A) tail length and site usage somewhat difficult to follow and the analysis rather cursory. The authors find no difference in polyA site usage in vir-1 at 17C or 27C (although both are different than WT). For Figure 7A, in addition to the histogram of poly A site shift, I would like to see a plot (heatmap?) that compares poly A sites shift for individual mRNAs across samples, instead of only aggregated data. Are there individual mRNAs that differ between 17 and 27C in vir-1?

A similar comment applies to the data in 7E. Please also compare individual mRNA polyA tail length across samples. What is the significance of the change in polyA tail length? The tails are shorter in vir-1 than Col at 27 C. But vir-1 has a very similar phenotype to WT at 27 C. At 17 C, vir-1 tails are longer than WT. Together, do these two results imply that polyA tail length is unlikely to be related to the observed phenotypes? In other words, if longer tails have no effect, do shorter tails? Is there any relationship between RNAs with altered polyA site usage or tail length and those mRNAs that are misexpressed in the mutant? Are immunity gene mRNAs more likely to be m6A modified than other mRNAs?

Minor comments

At times it felt like the authors were stretching to fill seven figure with data. For example, in Figure 1, it was not necessary to show the data on increased PR1 expression in 6 different sub panels (B-F) to convince the reader that PR1 expression was increased. A similar comment applies to Figure 3A-D. In Figure 3 please write the common gene names above the plots.

In Supplemental Table 3 the Enriched GO Terms tab is blank. Supplementary File 1 appeared to be missing from the submission, so I could not evaluate the sequencing statistics (# of reads per sample, mapping %, etc). Many of the Supplemental Tables would benefit from a readme that describes what analysis was performed and what the different columns mean.

Significance

The manuscript provides additional insight on the functional consequences of disrupting adenosine methylation in RNA, identifying features of an autoimmune response. Given the ubiquity of m6A in RNA across eukaryotes, this is a result that will be of interest to basic researchers in the plant RNA modification community and likely those working in other eukaryotes. However, the study is not able to connect the inappropriate expression of immune response genes back to the function m6A in RNA, and the effects might be indirect. Although there is speculation that RNA that lacks m6A might trigger autoimmunity, the presented experiments do not directly test that hypothesis (nor do the authors claim to).

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Reply to the Reviewers

I thank the Referees for their...

Referee #1

1. The authors should provide more information when...

Responses + The typical domed appearance of a hydrocephalus-harboring skull is apparent as early as P4, as shown in a new side-by-side comparison of pups at that age (Fig. 1A). + Though this is not stated in the MS 2. Figure 6: Why has only...

Response: We expanded the comparison

Minor comments:

1. The text contains several...

Response: We added...

Referee #2

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Referee #2

Evidence, reproducibility and clarity

Enterovirus genomes contain an AUG triplet at the 3'-border of the IRES, often far upstream of the initiation codon for the principal ORF that encodes the viral polyprotein. Prior in vitro and in vivo studies have shown that this upstream AUG triplet (uAUG) initiates translation of a short polypeptide ("UP") encoded by an upstream ORF (uORF) that promotes viral infection in gut epithelial cells (Refs. 5, 6). In the present thorough and rigorously controlled study, O'Connor et al. extend these observations, thereby providing further insights into the regulatory and coding potential of translation of in alternate reading frames in viral mRNAs.

They first undertook detailed analyses of almost 10000 enterovirus genomic sequences and determined that one third contained additional AUG triplets in the vicinity of the uAUG, collectively designated upstream uAUGs (uuAUGs), that could potentially initiate translation of uuORFs that are mostly very short but that in a few instances encode UP-related polypeptides.

Systematic studies involving (a) ribosomal profiling and (b) the use of a dual luciferase reporter system showed that uuAUG triplets are recognized by ribosomes in infected cells and are functional albeit inefficient initiation codons. The uuAUG triplet in the enterovirus CVA-13 (Flores strain) initiates translation of an 8aa-long non-UP-like peptide, and the functional importance of this uuAUG was assayed by substituting it by a GUG triplet to downregulate uuORF translation. This mutation had no effect of infection in HeLa cells, but the uuAUG-containing (wt) virus had a competitive advantage over the mutant in mixed mutant/wt infections in terminally differentiated neuronal cells and in differentiated human intestinal organoids. This differential effect was similar to the previously reported competitive advantage conferred by UP expression during enterovirus infection in differentiated cells (Ref. 5). The function of non-UP-like proteins initiating at uuAUG codons remains unknown. However, elimination of stop codons that modify their length of uORFs modulated upstream ORF expression, although the mechanism responsible for this effect remains unknown. These results suggest that the interplay between initiation, termination and recycling steps on the 5'UTR of enteroviruses has the potential to affect viral pathogenicity.

The data in the manuscript are strong, well controlled and validated. Elements of the manuscript could be presented more clearly.

Minor comments

1. Line 56. Domain 1 is a cloverleaf i.e. not just a stemloop.
2. Fig. 4A, 5B, 8C. It would be informative to add an additional 5'-terminal nucleotide to the structure of the SL-VI region to show the Kozak context of the uuAUG codon.
3. Figs. 8C, 8E, 8F. It might be more reader-friendly to replace structural models of sections of enterovirus 5'UTRs by a schematic representations to show uuORFs, uORFs, ppORFs etc and how altered stop codons affect their overlap. The corresponding section of the manuscript could also be presented in a more straightforward manner.
4. Lines 473-4. This statement is incorrect, because eIF4G is required for IRES-dependent initiation. 2A-mediated cleavage of eIF4G does not abrogate IRES function because it splits off the non-essential N-terminal (eIF4E-binding) region from the critical C-terminal region that binds directly to enterovirus IRESs and recruits eIF4A (Ref. 7; PMID: 19470487).
5. Ref. 27 is annotated incorrectly

Significance

The study reinforces and extends the authors' previous conclusions (Ref. 5, 13, 28, 31) that the genomes of positive-sense RNA viruses can and do have coding properties that are more complex than simply encoding a single open reading frame. Careful examination of a large panel of enterovirus genomes revealed a great diversity in coding potential, and the authors are right to suggest that further correlation of coding potential (particularly alternate ORFs/alternate reading frames) with pathogenic phenotypes is merited, particularly for variants of a single virus.

This study also provides insights into the influence of alternative upstream open reading frames on viral fitness using strong experimental models (viral infection of differentiated cells and organoids in addition to HeLa cells), and appropriate methods (e.g. an innovative competition assay to compare the competitive advantage of co-infecting variants of a virus, sophisticated reporter assays). Although the mechanistic basis for the influence of uuORFs on enterovirus infection of cells remains to be fully elucidated, these studies indicate that the topic strongly merits further study. In consequence, this report will be of interest both to molecular virologists and to scientists with an interest in gene expression mechanisms.

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Referee #1

Evidence, reproducibility and clarity

This study provides a detailed analysis of upstream and "upstream upstream" open reading frames in enteroviruses from the Cosackiepol and Alphacoxsackie species. The work includes a comprehensive bioinformatic analysis of uORF and uuORF diversity and conservation across the EVs, along with characterization of these ORFs by Riboseq and reporter assays. The authors also include a characterization of the uORFs through the mutation of these ORFs in both cell lines and iPSC derived cells.

The manuscript is detailed, the experiments rigorous, and their description clear. The work provides a number of orthogonal experiments to support the claims of the study.

Significance

General assessment: This work is of high quality, and an important addition to the literature on uORFs, though it doesn't provide much mechanistic insight into the function of these ORFs. It falls short in pushing our understanding of uORF function forward.

• I wonder if the authors can expand their studies to address the potential mechanisms by which these ORFs function, whether through their translation or translation products.
• Have the authors considered exploring the possible functions similar to cellular transcripts, e.g. what they reference in the discussion regarding ATF4, by modulating stress responses and assessing expression of uORF and ppORF? These studies would greatly enhance the additional insights the manuscript provides.
• A more comprehensive accounting of the ORF diversity across the EV's would be a valuable analysis. Are there ORFs in the negative strand (as have been characterized in influenza), or elsewhere in the positive strand, that may have functions?

In Fig. 7A: "iPCS" -> "iPSC"

Advance: This work builds on the authors' previous characterization of the uORFs of related EV's. It provides further support consistent with their previous findings that these uORFs are of importance of these regions in the replication of the virus, especially in differentiated target tissues, suggesting they contribute to the pathogenesis of the virus as part of the known important role the IRES regions are known to play. How the translation, or the products of translation, function to confer this phenotype remains elusive.

Audience: This will be of interest to virologists working on cryptic translational elements in viruses, which are found in many viruses, and sure to be discovered in more as we begin to appreciate their important role, however the findings are not likely to be especially relevant to very broad audience.

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Reply to the reviewers

We appreciated the constructive suggestions from the reviewers, and the explanation of the contribution of the manuscript. We have revised the manuscript in accordance with their suggestions, as discussed below.

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __ This manuscript presents a computational analysis of PRC1, a passive microtubule crosslinker important for cell division, with a focus on its role in resisting force generation within antiparallel bundles, whose sliding is promoted by active kinesin motors. Using a previously developed simulator and several assumptions, the authors successfully recapitulated the two modes of PRC1 sliding resistance - coasting and braking - that were previously observed in in vitro reconstruction assays. The simulation also reproduces the redistribution of PRC1 within the overlap region as microtubules transition into the braking mode, a phenomenon also observed experimentally. An interesting outcome of the simulation is the change in spacing between the microtubules: The distance narrows as the sliding polymers switch from the coasting to the breaking mode, associated with an increased tilt of PRC1.

Major comments: I find that this manuscript makes a valuable contribution to the cytoskeletal community, as the role of interfilament spacing in polymer assembly has been relatively underexplored, except for more classic studies such as those on muscle contraction and flagellar beating. What I had difficulty fully visualizing the model was the behavior of PRC1 during the coasting and braking modes. In my understanding, if individual heads of PRC1 bind and unbind to and from microtubules while microtubules that they crosslink slide apart, PRC1 should experience greater stretching and thus tilt more at higher sliding speeds. When the sliding slows down, the relative polymer position changes less within a given time, and PRC1 unbinding and re-binding would more easily reset their tilt to an equilibrium angle. However, the authors' simulation shows the opposite: PRC1 exhibits a greater tilt during the braking mode. This seems counterintuitive and a more detailed description and interpretation would worth. I suggest that the authors include a schematic illustrating the configuration of individual PRC1 molecules (e.g., angle and stretch) within the ensemble, particularly during their transition phase. This would greatly help readers grasp how this important protein ensemble switches its mechanical mode depending on polymer sliding and geometry.

We thank the reviewer for the comments on the contribution of the results of the manuscript. Braking typically initiates at higher sliding speeds, when PRC1 do experience greater stretching and tilt more as the reviewer writes. As sliding slows down, the ability of PRC1 to unbind, re-bind, and rest their tilt to the equilibrium angle is restricted by the small distance between the microtubules: PRC1 binding will tend to occur tilted in the direction of sliding, and molecules tilted in this direction promote close separations, keeping overlaps braking. To clarify why braking overlaps are stable we added text and figure 4H. Steric interactions within the clusters at the overlap edges also restrict rebinding. To illustrate the behavior of PRC1 molecules during the transition from coasting to braking , we have added in figure 4A a schematic derived from simulation data of the microtubule and PRC1 positions, separations, and tilts during the transition from coasting to braking.

Minor comments: 1. How was the bimodal velocity distribution (Fig. 1D) obtained experimentally? Were the individual data averaged over time from the start to the end of individual sliding events? If so, does mode switching within a pair lead to under/over-estimate of the coasting and braking speeds?

These data are reproduced from Alfieri et al. Current Biology 2021. In that paper, we acquired this data by observing the sliding separation of PRC1-crosslinked microtubule pairs and recorded two distinct velocities for each pair: the “bundled” velocity when overlap>0 and PRC1 was engaged in crosslinking and then the “escaped” velocity once the two microtubules had separated. In the vast majority of cases (>90%) each of these velocities was well measured by fitting a slope to the kymograph, as there were only very minor deviations from a linear position-versus-time relationship (e.g. we rarely saw acceleration or deceleration within an individual pair). In the rare (

Line 158 includes typo.

We thank the reviewer for pointing out this typo, which has been corrected.

The fixed-separation simulation in Fig. 3D is important for demonstrating the causality. How was the average speed (V_avg) calculated in this case? Specifically, do microtubule pairs that slide at coasting mode maintain a high speed over the entire sliding event when the inter-filament spacing is fixed at a large distance?

We thank the reviewer for raising this point, which was not clear in the original manuscript. In the fixed-separation simulation of Fig 3D the average speed is calculated for the whole simulation. We have clarified this in the figure 3 caption. We have also added a supplementary figure showing the velocity distribution. The coasting pairs do maintain high speed over the event.

In my understanding, the attractive and repulsive lateral forces exerted by PRC1 with positive and negative tilts arise because PRC1 has a natural tilt relative to the perpendicular. Is this correct? It would be helpful to illustrate this assumption in a figure to clarify the molecular behavior being modelled.

The reviewer raises an important point that we have clarified in the revised manuscript. The linear (spring stretch/compression) force is the primary contributor to the attractive lateral force in both braking and coasting states. The torsional force that arises from the natural tilt of PRC1 does contribute significantly to repulsion between microtubules in the coasting state. We have clarified this in the text and added a supplementary figure showing the energy and forces from PRC1 molecules as a function of angle.

In the paragraph starting from line 258, the authors discuss Ase1 and the yeast spindles. What is the relevance to PRC1 particularly in considering that Ase1 exerts an entropic force within the confined microtubule bundles to resist sliding (e.g., Lasky et al., 2015)?

We thank the reviewer for raising this important point. It is true that Ase1 has been shown to generate entropic forces that work to push against microtubule sliding, while this specific behavior has not been observed for PRC1. We believe that such forces are likely to arise when Ase1 is in a coasting-like mode and the individual crosslinkers are free to diffuse within the confines of the overlap, which is the mechanism Lansky et al. propose. In this paragraph of the discussion, we are highlighting the experimental observation that microtubule-microtubule spacing significantly reduces as a yeast cell proceeds from metaphase to anaphase, with late anaphase MT separations measured to be ~15nm, similar to what we predict for microtubule pairs that have engaged in a braking mode. We therefore speculate that a coasting-to-braking transition may be more generally applicable across different spindle types, at least when involving MAP65 family members such as Ase1 and PRC1. In the yeast spindle, then, we speculate that when microtubule separation is larger, Ase1 would be arranged in a coasting-like mode of binding, capable of generating entropic forces. Later, it is possible the molecules switch to a more braking-like mode, where MT-MT spacing reduces significantly as shown in EM data from yeast spindles. It will be useful in the future to acquire similar data from mammalian spindles to determine if late anaphase midzone separation also compacts when PRC1 is present, which would further validate our predictions. We have clarified the discussion of this point in the revision.

Fig. 1B, C would benefit from additional labels, as the colors in the images do not match those in the accompanying cartoon.

We thank the reviewer for the suggestion, and have added additional labels.

Reviewer #1 (Significance (Required)):

As in my major comments above. My expertise is experimental biophysics on microtubules and motors.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __The paper presents simulations of sliding antiparallel microtubules linked by PRC1 crosslinking proteins. It aims to reproduce and explain experimental observations by Alfieri et al. that suggested that PRC1 could adopt two distinct modes of resistive force production against kinesin-driving sliding forces.

The model which the authors propose is that antiparallel sliding leads to the accumulation of PRC1 at the edges, which results in higher tilt angles of PRC1 molecules and consequently smaller microtubule separation. In the higher tilt regime PRC1 can exert more braking forces since, its angle with the Microtubules is smaller. To my understanding the key parameters for this model to work it the spontaneous tilt angle, and torsional spring that PRC-1's structure encodes. The authors demonstrates that for reasonable values very good agreement with experimental observations can be reached. The simulations are done in the CYlAks framework, which the Betterton group developed and validated in earlier work. The discussion is clear and readable

Major Comment: While the paper goes at great length to successfully reproduce experiments, it is not discussed how sensitive the model is to changes in parameters. In particular it remains unclear how sensitive the model is to changes in the torsional spring that is being used to model PRC-1. Given that this is key to the findings presented here, I would have hoped for a more extensive discussion of the relevant physics. In particular It should be discussed how non-linearities and asymmetries in the torsional spring would affect the phenomenon identified here.

We appreciate the reviewer’s suggestion to examine sensitivity to variation in model parameters. We note that we do present in Figure 2 a smaller exploration of parameter space; when key values are modulated by an order of magnitude, we find differences in the simulated outputs (e.g. enhanced or reduced tip clustering in response to changes in MAP diffusion or end binding). We also note the supplementary information includes the effect of varying parameters including the strength and asymmetry of the torsional spring, which addresses the specific concern noted. Given the length of the current manuscript, we propose to delay a more extensive study of parameter sensitivity to future work.

(Very) Minor remark: the orientation of PRC-1 molecules is inconsistent between figures.

We thank the reviewer for pointing this out. We have edited the figures to make the orientation consistent.

__Reviewer #2 (Significance (Required)): __ PRC-1 is an important cross-linking protein in cell division, and its mechanics is at the center of much current research interest. As such this paper is timely. The key physics that is interesting here is the link between geometry, PRC1-arrangements and geometry of the MT network. The authors reproduce successfully the experimental observations, with reasonable parameters. But a parameter study that exposes the physics at play, and would help the reader generalize the concepts at play is missing.

In its current state the paper will be of interest to experimentalists and theoreticians working on cytoskeletal filament networks. But it could be even more so, if the authors sought to generalize beyond the experiment at hand.

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

The manuscript by Steckhahn and colleagues is a computational study of the mechanics of microtubule interactions with an essential mitotic crosslinker, PRC1. PRC1 is known to act as a molecular clutch, resisting the sliding of antiparallel microtubules in order to maintain mitotic spindle integrity. The present study aims to explain the recently discovered two modes of action of this clutch: a weakly resistant 'coasting' mode and a highly resistant 'braking' mode. The authors employ their previously developed Cytoskeleton Lattice-based Kinetic Simulator (CyLaKS) model to carry out Monte Carlo/Langevin dynamics simulations of microtubule sliding, driven by a mitotic kinesin and resisted by an ensemble of PRC1 crosslinkers, with explicit account of their diffusion, binding-unbinding kinetics, stretching-compression, and volume-exclusive interactions. Their reasonable model successfully reproduces the bimodal distribution of microtubule sliding rates, and offers a simple explanation of the two modes of action of the crosslinkers. According to the authors' conclusion, in the coasting mode PRC1 molecules are almost perpendicular to the microtubules, while the microtubules are separated by about 30 nm (close to the rest length of PRC1). When the overlap between the sliding microtubules shrinks, the PRC1 molecules cluster, which facilitates their tilting. This has two effects: a projection of force bringing microtubules closer together appears, and a projection of resistive force along the microtubule axis becomes substantial, enabling more efficient 'braking'.

The key conclusions are convincing, clearly stated, and supported by data. The simulation techniques are justified and well described. I have no concerns about the technical side of this study.

We thank the reviewer for their clear summary of the results of the paper.

Reviewer #3 (Significance (Required))

I believe this is a useful piece of work, which clarifies some important aspects of the PRC1 mechanism of action by showing that a simple but rigorous mechanical consideration is sufficient to explain the observed bimodal behavior of the mitotic crosslinkers. The findings could be interesting to biophysicists and cells biologists, interested in cytoskeleton and cell division.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Steckhahn and colleagues is a computational study of the mechanics of microtubule interactions with an essential mitotic crosslinker, PRC1. PRC1 is known to act as a molecular clutch, resisting the sliding of antiparallel microtubules in order to maintain mitotic spindle integrity. The present study aims to explain the recently discovered two modes of action of this clutch: a weakly resistant 'coasting' mode and a highly resistant 'braking' mode. The authors employ their previously developed Cytoskeleton Lattice-based Kinetic Simulator (CyLaKS) model to carry out Monte Carlo/Langevin dynamics simulations of microtubule sliding, driven by a mitotic kinesin and resisted by an ensemble of PRC1 crosslinkers, with explicit account of their diffusion, binding-unbinding kinetics, stretching-compression, and volume-exclusive interactions. Their reasonable model successfully reproduces the bimodal distribution of microtubule sliding rates, and offers a simple explanation of the two modes of action of the crosslinkers. According to the authors' conclusion, in the coasting mode PRC1 molecules are almost perpendicular to the microtubules, while the microtubules are separated by about 30 nm (close to the rest length of PRC1). When the overlap between the sliding microtubules shrinks, the PRC1 molecules cluster, which facilitates their tilting. This has two effects: a projection of force bringing microtubules closer together appears, and a projection of resistive force along the microtubule axis becomes substantial, enabling more efficient 'braking'. The key conclusions are convincing, clearly stated, and supported by data. The simulation techniques are justified and well described. I have no concerns about the technical side of this study.

Significance

I believe this is a useful piece of work, which clarifies some important aspects of the PRC1 mechanism of action by showing that a simple but rigorous mechanical consideration is sufficient to explain the observed bimodal behavior of the mitotic crosslinkers. The findings could be interesting to biophysicists and cells biologists, interested in cytoskeleton and cell division.

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Referee #2

Evidence, reproducibility and clarity

The paper presents simulations of sliding antiparallel microtubules linked by PRC1 crosslinking proteins. It aims to reproduce and explain experimental observations by Alfieri et al. that suggested that PRC1 could adopt two distinct modes of resistive force production against kinesin-driving sliding forces.

The model which the authors propose is that antiparallel sliding leads to the accumulation of PRC1 at the edges, which results in higher tilt angles of PRC1 molecules and consequently smaller microtubule separation. In the higher tilt regime PRC1 can exert more braking forces since, its angle with the Microtubules is smaller. To my understanding the key parameters for this model to work it the spontaneous tilt angle, and torsional spring that PRC-1's structure encodes. The authors demonstrates that for reasonable values very good agreement with experimental observations can be reached. The simulations are done in the CYlAks framework, which the Betterton group developed and validated in earlier work. The discussion is clear and readable

Major Comment:

While the paper goes at great length to successfully reproduce experiments, it is not discussed how sensitive the model is to changes in parameters. In particular it remains unclear how sensitive the model is to changes in the torsional spring that is being used to model PRC-1. Given that this is key to the findings presented here, I would have hoped for a more extensive discussion of the relevant physics. In particular It should be discussed how non-linearities and assymetries in the torsional spring would affect the phenomenon identified here.

(Very) Minor remark: the orientation of PRC-1 molecules is inconsistent between figures.

Significance

PRC-1 is an important cross-linking protein in cell division, and its mechanics is at the center of much current research interest. As such this paper is timely. The key physics that is interesting here is the link between geometry, PRC1-arrangements and geometry of the MT network. The authors reproduce successfully the experimental observations, with reasonable parameters. But a parameter study that exposes the physics at play, and would help the reader generalize the concepts at play is missing.

In its current state the paper will be of interest to experimentalists and theoreticians working on cytoskeletal filament networks. But it could be even more so, if the authors sought to generalize beyond the experiment at hand.

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

This manuscript presents a computational analysis of PRC1, a passive microtubule crosslinker important for cell division, with a focus on its role in resisting force generation within antiparallel bundles, whose sliding is promoted by active kinesin motors. Using a previously developed simulator and several assumptions, the authors successfully recapitulated the two modes of PRC1 sliding resistance - coasting and braking - that were previously observed in in vitro reconstruction assays. The simulation also reproduces the redistribution of PRC1 within the overlap region as microtubules transition into the braking mode, a phenomenon also observed experimentally. An interesting outcome of the simulation is the change in spacing between the microtubules: The distance narrows as the sliding polymers switch from the coasting to the breaking mode, associated with an increased tilt of PRC1.

Major comments:

I find that this manuscript makes a valuable contribution to the cytoskeletal community, as the role of interfilament spacing in polymer assembly has been relatively underexplored, except for more classic studies such as those on muscle contraction and flagellar beating. What I had difficulty fully visualizing the model was the behavior of PRC1 during the coasting and braking modes. In my understanding, if individual heads of PRC1 bind and unbind to and from microtubules while microtubules that they crosslink slide apart, PRC1 should experience greater stretching and thus tilt more at higher sliding speeds. When the sliding slows down, the relative polymer position changes less within a given time, and PRC1 unbinding and re-binding would more easily reset their tilt to an equilibrium angle. However, the authors' simulation shows the opposite: PRC1 exhibits a greater tilt during the braking mode. This seems counterintuitive and a more detailed description and interpretation would worth. I suggest that the authors include a schematic illustrating the configuration of individual PRC1 molecules (e.g., angle and stretch) within the ensemble, particularly during their transition phase. This would greatly help readers grasp how this important protein ensemble switches its mechanical mode depending on polymer sliding and geometry.

Minor comments:

1. How was the bimodal velocity distribution (Fig. 1D) obtained experimentally? Were the individual data averaged over time from the start to the end of individual sliding events? If so, does mode switching within a pair lead to under/over-estimate of the coasting and braking speeds?
2. Line 158 includes typo.
3. The fixed-separation simulation in Fig. 3D is important for demonstrating the causality. How was the average speed (V_avg) calculated in this case? Specifically, do microtubule pairs that slide at coasting mode maintain a high speed over the entire sliding event when the inter-filament spacing is fixed at a large distance?
4. In my understanding, the attractive and repulsive lateral forces exerted by PRC1 with positive and negative tilts arise because PRC1 has a natural tilt relative to the perpendicular. Is this correct? It would be helpful to illustrate this assumption in a figure to clarify the molecular behavior being modelled.
5. In the paragraph starting from line 258, the authors discuss Ase1 and the yeast spindles. What is the relevance to PRC1 particularly in considering that Ase1 exerts an entropic force within the confined microtubule bundles to resist sliding (e.g., Lasky et al., 2015)?
6. Fig. 1B, C would benefit from additional labels, as the colors in the images do not match those in the accompanying cartoon.

Significance

As in my major comments above. My expertise is experimental biophysics on microtubules and motors.

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Reply to the reviewers

Firstly, we would like to thank the reviewers for their time and efforts in critiquing this paper. The reviewers addressed our study to be significant, but also presented great suggestions to improve our manuscript, mainly the comparison of mRNA and eRNA for predicting subtype specificity and prognosis, the integration with independent validation datasets, etc. Our preliminary analyses showed that our classified mRNAs can predict subtypes better which is not surprising, as these subtypes were initially discovered using mRNA differences. Hence, we employed a novel approach of associating these classified mRNA and eRNA with distance and identified 71% classified eRNAs are associated with classified mRNAs. We also propose to integrate the datasets with PEGS (Briggs et al 2021) to achieve better mRNA-eRNA association and Perturb-seq validated regions to achieve functional validation of the eRNA loci. We believe that our potential improved integrative analyses will improve the novelty and power of our findings, as this is an unique approach which is employed in patient samples-based high resolution eRNA atlas for the first time. We have addressed most of the other major and minor comments of the reviewers and have provided the preliminary revised manuscript.

Reviewer #1

Evidence, reproducibility and clarity

Summary<br /> This study assesses eRNA activity as a classifier of different subtypes of breast cancer and as a prognosis tool. The authors take advantage of previously published RNA-seq data from human breast cancer samples and assess it more deeply, considering the cancer subtype of the patient. They then apply two machine learning approaches to find which eRNAs can classify the different breast cancer subtypes. While they do not find any eRNA that helps distinguish ductal vs. lobular breast cancers, their approach helps identify eRNAs that distinguish luminal A, B, basal and Her2+ cancers. They also use motif enrichment analysis and ChIP-seq datasets to characterize the eRNA regions further. Through this analysis, they observe that those eRNAs where ER binds strongest are associated with a poor patient prognosis.

Major comments:

Part of the rationale for this study is the previous observation that eRNAs are less associated with the prognosis of breast cancer patients in comparison to mRNAs and they claim that the high heterogeneity between breast cancer subtypes would mask the importance of eRNAs. In this study, the authors solely focus on eRNAs as a classification of breast cancer subtypes and prognostic tool and do not answer whether eRNAs or mRNAs are a better predictor of cancer subtypes and of prognosis. Since the answer and the tools are already in their hands, it would be important to also see a comparative analysis where they assess which of the two (mRNAs or eRNAs) is a better predictor.

Response: We appreciate the reviewer for this valid point about comparing the prognostic eRNAs vs mRNAs. Our study doesn’t imply that eRNA markers are better than mRNAs in predicting subtype specificity and/or prognosis, but our motivation for working with eRNAs is that they can be used to define relevant transcriptional regulators and prognosis generally if they are subtyped. As the molecular subtypes in breast cancers were established using gene expression datasets, mRNAs would perform better as predictors of subtypes and or prognosis. However, identifying regulatory networks with emphasis on transcription factor binding motif analyses is not achievable using mRNA datasets. Analysing the active enhancer regions with eRNA transcription will provide high resolution landscape of TF and epigenetic networks. These sorts of analyses usually require ATAC-seq or H3K27ac datasets, but these assays need fresh frozen tissue material and laborious experimental designs compared to RNA-seq datasets. Furthermore, eRNA-transcribing enhancers represent highly active enhancers, while ATAC and H3K27ac datasets can identify all enhancers, which can be inactive or poised, but captured due to the dynamic nature of enhancers. We demonstrate that traditional RNA-seq datasets mapped on active enhancer regions showing eRNA transcription would be sufficient to identify the highly active TF network and gene-enhancer regulatory frameworks in a subtype-specific manner, hence emphasising the potential of eRNA studies.

Hence, the scope of our study is not to establish which RNA can predict subtype and survival, but to demonstrate the potential of studying eRNAs in patient samples using traditional RNA-seq assays. This study would be beneficial for epigenetics biologists of how enhancer transcription can be associated with gene regulation through deregulated transcription factor networks in patients. The above section had been included in the discussion in the revised manuscript.

As the comparative analyses suggested by the reviewer will substantiate the potential of eRNAs being studied as cancer prognostic markers, we performed identical methodologies with our machine learning approaches on the published TCGA mRNA-seq datasets, identify the subtype-specific mRNAs as well as prognostic mRNAs and perform the comparative analyses of eRNAs and mRNAs. As we expected, mRNAs indeed perform better in associating with subtype specificity than eRNAs as we could identify more subtype-specific mRNAs with better statistics metrics. The results exhibit great separation across subtypes (Basal, Her2, LumA/B) as well as Ductal vs Lobular.

We believe that eRNA and mRNA are complementary but not comparative to predict subtype-specific survival. To address this in the revised manuscript, we performed an initial selection of the eRNAs associated with their corresponding subtype-specific mRNAs within 50 kb distance which can be integrated with the above analyses, based on the suggestion from reviewer 3. In our preliminary analysis, around 71% of eRNAs are associated with the subtype-specific mRNAs and we also observed an observable separation of ductal and lobular subtypes using this method.

Furthermore, we integrated our enhancer RNAs with the key enhancer regions which show significant impact on gene transcription, as shown in single cell CRISPRi screens (Perturb-seq) datasets derived from ATAC-matched H3K27ac datasets verified on one ER+ and one ER- breast cancer cell lines (Wang et al., Genome Biology 2025, https://genomebiology.biomedcentral.com/articles/10.1186/s13059-025-03474-0) . Our initial analyses identified at least 29 regions from the Perturb-seq datasets overlapping with 72 and 5 eRNAs of subtype classification and Her2 survival respectively.

For the revised manuscript, we will perform the mRNA-eRNA association in a detailed manner and include the data. We will also employ our well-established tool for associating mRNAs and noncoding elements, Peak set Enrichment in Gene Sets (PEGS, Briggs et al., F1000 research, 2021 https://f1000research.com/articles/10-570/v2 ). We hypothesise that this will improve the power of the classification models used in the study and will also provide gene-enhancer RNA interaction landscape in patient samples for the first time. Furthermore, we will integrate the activity of these eRNA-mRNA pairs with chromatin accessibility and enhancer activity using ATAC-seq and H3K27ac ChIP-seq datasets to establish more robust active regulatory networks in patient samples. We will also perform motif analyses on the published ATAC-seq peaks (performed on TCGA-BRCA patient samples, Corces et al., 2018) close to the eRNA loci to identify the TF networks with better precision, hopefully unravelling novel and relevant subtype-specific TFs in an efficient manner, better than our original work. Furthermore, as an experimental functional validation of our classified eRNAs, we will investigate the regulatory effect of 29 Perturb-seq overlapped regions. Hence, our revised manuscript will potentially provide a comprehensive validated list of enhancer RNA regions which are highly active, actively transcribing, subtype and survival specific regulatory networks in breast cancer patients for the first time.

The authors run the umaps of Fig. 1C only taking the predictor eRNAs. It is then somewhat expected to observe a separation. Coming from a single-cell omics field, what I would suggest is to take the eRNA loci and compute a umap with the highly variable regions, perform clustering on it and assess how the cancer subtypes are structured within the data. This would give a first overview of how much segregation and structure one can have with this data. Having a first step of data exploration would also strengthen the paper. If the authors have tried it, could the authors comment on it?

Response: We appreciate the reviewer for sharing their experience from single cell omics analysis. In our case, following the scRNA like pipeline is not appropriate, given the focus of our study on identifying markers on the already annotated subtypes. Basically, we aim to assess the quality of the identified markers (the quality is quantified by the statistics provided for random forest classification), and we see that the data is well-separated in PCA using only PC1 and PC2. We showed the umap (using PC1 and PC2) for better visualization in the original manuscript and we included the PCA plots in the revised manuscript.

'neither measures could classify any distinct eRNAs for invasive ductal vs lobular cancer samples' S1B. Just by eye, I can see a potential enrichment of ductal on the left and on the right while lobular stays in the center. This suggests to me that, while perhaps each eRNA alone does not have the power to classify the lobular vs ductal subtype, perhaps there is a difference - which could result from a cooperative model of eRNA influence - that would need further exploration. Would a PCA also show enrichments of ductal vs. lobular in specific parts of the plot? It may be worth exploring the PC loadings to see which eRNAs could play an influence. In this regard, a more unbiased visual examination, as suggested in my previous point, could help clarify whether there could be an association of certain eRNAs that cannot be captured by ML.

Response: The subtypes of cancer patients (Basal, Her2, LumA/B) possess clear differences in mRNA expression in breast cancer studies. Given the fixed annotations of the subtypes in the patient datasets, we applied our methodologies on mRNA datasets, and the results exhibited great separation across subtypes (Basal, Her2, LumA/B) as well as Ductal vs Lobular. In addition, 70% of subtype-specific eRNAs are located next to mRNA. This ensures that we detected proper eRNA markers. Furthermore, Random Forest is the standard and powerful non-linear classifier for these types of classifying questions. Therefore, we hypothesized that the data which can distinguish Ductal vs Lobular does not exist in the used eRNA dataset. We only detected 38 subtype-specific mRNAs using information gain with standard cutoff 0.05 which they have classifying power across ductal-lobular. With this standard cutoff only one eRNA-associated gene was detected. To explore more, we used low cutoff for information gain (0.01) and then took only the eRNAs which are located near classified mRNAs (up to 50KB). In this way, we detected 96 eRNA candidates linked to 8 classified mRNAs. These 96 eRNAs could, to some extent, classify ductal vs lobular (PCA plots attached above). This observation can further verify that if a more comprehensive eRNA dataset exists, we could detect better eRNA markers and cover more (probably all) mRNA markers. Hence, cooperative model of eRNA as suggested by the reviewer can't be achieved and random forest is one of the efficient tools to decipher the cooperation if it exists. Besides, as we demonstrated in this paper that eRNA is a complementary dataset to mRNA which can assist in the identification of regulatory networks. For the revision, we will provide more detailed eRNA-mRNA associations using integration with PEGS and Perturb-seq validated regions, in both subtype classification and survival and will motivate the potential similar studies for ductal vs lobular in the discussion.

"we employed machine learning approaches on 302,951 eRNA loci identified from RNA-seq datasets from 1,095 breast cancer patient samples from previous studies" - the previous studies from which the authors take the data [11,12] highlight the presence of ~60K enhancers in the human genome and they use less than that in their analysis. Could the authors please clarify the differences in numbers with previous studies and give a reasoning?

Response: ~300K enhancers are derived from ENCODE H3K27ac datasets which represents all active enhancer regions marked by H3K27ac (Hnisz et al., 2013). This is a high-resolution map of eRNA loci ever presented. In Chen et al 2020, 1,531 superenhancers representing 30K eRNA loci was utilised for exploratory analysis, and the findings were generalised back to the 300K set. 65K enhancer loci covers tissue-specific enhancers initially identified by FANTOM CAGE datasets and this subset provide limited regions of eRNA expression. Hence, our analyses on ~300K eRNA loci provide unbiased information on subtype specificity and gene-TF regulatory networks. The differences had been highlighted in the methods and results in the revised manuscript.

Also, from the methods section, they discard many patient samples due to low QC, so, from what I understand, the number of samples analyzed in the end is 975 and not 1,095.

Response: We thank the reviewer for pointing this out and we have updated the numbers in the revised manuscript.

Minor comments:

• Can the authors please state the parameters of the umap in methods? Although it could be intrinsic to the dataset, data points are grouped in a way that makes me think that the granularity is too forced. Could the authors please show how the umap would behave with more lenient parameters? Or even with PCA?

Response: We used ‘umap’ function from umap package (with default parameters) in R using only PC1 and PC2, hence the granularity is not forced. As suggested by the reviewer, we have now added PCA plots in the main figures (Fig. 1E) and moved all the umap plots to the Supplementary figures (Fig.S1B) in the revised manuscript.

• 'Majority of the basal' -> The majority of the basal.

Response: We thank the reviewers for noticing the typo and we corrected this in the revised manuscript.

Significance

This is a paper relevant in the cancer field, particularly for breast cancer research. The significance of the paper lies in digging into the breast cancer samples, taking the different existing subtypes into account to assess the contribution of eRNAs as a classifier and as a prognostic tool. The data is already available but it has not been studied to this degree of detail. It highlights the importance of characterizing cancer samples in more depth, considering its intrinsic heterogeneity, as averaging across different subtypes would mask biology. My expertise lies in gene regulation and single-cell omics. My contribution will therefore be more focused on the analysis and extraction of biological information. The extent of its specific relevance in cancer research falls beyond my expertise.

Response: We appreciate the reviewer for understanding our efforts to bring out the importance of subtyping and to explore the association of eRNA in breast cancer transcriptional gene regulatory networks.

Reviewer #2

Evidence, reproducibility and clarity

Summary<br /> Enhancer RNAs (eRNAs) are early indicators of transcription factor (TF) activity and can identify distinct molecular subtypes and pathological outcomes in breast cancer. In this study, Patel et al. analysed 302,951 polyadenylated eRNA loci from 1,095 breast cancer patients using RNA-seq data, applying machine learning (ML) to classify eRNAs associated with specific molecular subtypes and survival. They discovered subtype-specific eRNAs that implicate both established and novel regulatory pathways and TFs, as well as prognostic eRNAs -specifically, LumA and HER2-survival- that distinguish favorable from poor survival outcomes. Overall, this ML-based approach illustrates how eRNAs reveal the molecular grammar and pathological implications underlying breast cancer heterogeneity.

Major comments

1. The authors define 302,951 eRNA loci based on RNA-seq data, yet it is widely known that many enhancers reside in proximity to promoters or within intronic regions (examples presented in Fig. 3B and S3). Consequently, it seems likely that reads mapped to these regions might not truly represent eRNA signals but include mRNA contamination. Could the authors clarify how they ensured that the identified eRNAs were not confounded by mRNA reads? What fraction of these enhancer loci is promoter proximal or intronic? How does H3K4me3, a well-established and standardized active promoter histone mark, behave on these loci? The reviewer considers it important to confirm that the identified eRNAs are indeed of enhancer origin rather than promoter transcripts.

Response: For this study, we utilised pan cancer atlas-based published work (Chen et al 2018 and 2020) where the abundant RNA signals on intronic and intergenic regions are included, and promoter-based signals are excluded. These studies utilise the advantage of identifying eRNAs on large sample size and the possibility of mRNA being on introns in 1000s of patient samples is very low. A clarification of this concern had been discussed in the Introduction of these studies as follows: “because eRNA reads associated with real enhancer activity recurrently accumulate, whereas background transcription noise tends to occur stochastically. The large number of RNA-seq reads obtained would compensate for the statistical power compromised by the low eRNA expression level typically observed in a single sample.” We included clarification of this concern in the discussion. Furthermore, as per the reviewer’s suggestion, we examined the distribution of the eRNA loci across the genome and found that majority of eRNA regions are located on introns and intergenic regions. This figure had been included in the Supplementary Fig. S6A.

2. In Fig. 1B, the F measure (0.540) of the Basal subtype using the Logmc method contradicts its extremely high precision (1.000) and sensitivity (0.890). The authors need to clarify the exact formula or method used to compute F1 and the discrepancy in the reported metrics for this subtype and perhaps other subtypes as well.

Response: We apologise for the mistake in this section and thank the reviewer for pointing this out. We included the formulas for each statistical metric in the method section of the manuscript. The F-measure was mentioned wrong which led to the confusion here. The figure had been corrected with the F-measure of 0.94 in the revised manuscript.

3. As shown in Fig. 4C, S4B, and most, if not all, tracks of Fig. S3, ER binding regions are not annotated as eRNA loci. It seems, in this reviewer's opinion, very unlikely that this is because they generally lack eRNA expression, but rather they do not express polyadenylated eRNA (typically 1D eRNA), which is captured in this dataset. The reviewer posits that these enhancers produce more transient, non-polyadenylated 2D eRNA. It has been widely documented in prior studies that ER-bound enhancers exhibit bimodal eRNA expression patterns [e.g., Li, W. et al. Functional roles of enhancer RNAs for oestrogen-dependent transcriptional activation. Nature 498, 516-520 (2013)]. Could the authors address this opinion and elaborate on how the restriction to polyadenylated transcripts might underrepresent enhancers regulated by ER and other TFs and whether this bias impacts the overall findings?

Response: The authors appreciate the reviewer’s suggestion to address the caveats of using polyadenylated eRNAs to identify the ER binding patterns. TCGA eRNA atlas with polyadenylated eRNAs indeed possesses this disadvantage of using polyadenylated eRNAs for this study, however currently there are no data available with bidirectional transcripts in any breast cancer patient samples. The tools to profile these RNAs are not robust enough to be performed on frozen cancer tissue samples which are extremely limited in their size and availability. By utilising the polyadenylated eRNA-seq datasets, we might not only lose the accuracy of ER binding patterns, but also for other transcription factors which activate/associate with bimodal expression around enhancers. However, our integrative analysis on stable polyadenylated eRNA loci can still identify the most-relevant TF networks of each subtype.

Furthermore, we validated this finding by analysing our own datasets of KAS-seq which represents any active transcribing bidirectional enhancers from MCF7 cell line. Independently, we also incorporated ATAC-seq, H3K27ac ChIP-seq, CAGE and GRO-seq data on the gene profiles in Fig. S3 to associate the eRNA regions identified in polyadenylated RNA datasets with ER binding sites in patients and published bidirectional transcripts in the preliminarily revised manuscript. We observed that all the ER binding sites are accompanied by open and active enhancer marks with bidirectional transcription (either GRO- or CAGE positive) but they are not on the exact location of eRNA regions. Subtype-specific eRNA regions close to genes like MLPH and XBP1 possess both active bidirectional transcribing ER bound sites far away (around 1.5 kb) from subtype-specific eRNA loci and bidirectional transcribing ER unbound sites. However, these distal ER binding sites are close to the regions from the list of 300K eRNA loci and they were simply not identified as subtype-specific regions. Hence, it can be true that the occupancy of ER might not be present on all subtype-specific eRNA loci, but our subtype-specific eRNA sites are representative of bidirectional transcription.

Upon the suggestion from the reviewer, we discussed the potential of identifying TF networks by analysing the 1D eRNAs, in the revised manuscript.

4. Despite the unsatisfied performance of the ML approach on classifying Her2 subtypes, the hierarchical clustering performed in Fig. 2A and S2A appears to show a reasonable separation of Her2 subtypes, showing as a clustered green band. Could the authors quantitatively assess how effective this clustering results and compare that to the ML outcome? (OPTIONAL)

Response: The authors acknowledge this interpretation from the reviewers. Using both the measures, our ML platform can identify markers for Her2 subtype but some of the statistical metrics are poor. As the heatmaps were performed based on these identified Her2 markers, a separate analysis on this cluster would not be much informative. The poor metrics for Her2 classification was already justified, partly due to the low number of Her2+ patients in the cohort.

5. In Fig. 4 and S4, the authors reported to have enriched binding or motif of TFs, e.g., FOXA1, AP-2, and E2A, specifically at enhancer loci with low eRNA level, which conflicts with their established roles as transcriptional activators. The reviewer asks for an address as to why these factors would be associated with basal low-eRNA regions and whether any additional data might clarify their functional role in these contexts.

Response: The authors appreciate the reviewer’s concern, but we would like to clarify that eRNAs which are less expressed in basal subtype are classified as basal low. These regions show high expression in luminal patients. Hence, there is a strong overlap of basal low and luminal high regions. FOXA1 and AP2 factors are strongly established coactivators in luminal ER+ transcriptional signaling, hence they are associated with basal low eRNA regions. We clarified this in the discussion and provided more literature evidence in the revised manuscript to demonstrate the strong role of FOXA1 and AP2 factors in ER+ luminal breast cancer transcriptional response.

6. Regarding Fig. 4B, the authors state that "ER binding occupies only the strongest ssDNA and GRO-seq-positive sites". Firstly, the GRO-seq data quality is poor with indiscernible peaks. This may be insufficient for a qualified representation of nascent eRNA expression. More importantly, it appears each heatmap is ranked independently, so top loci for ssDNA are not necessarily top loci for GRO-seq, ER, Pol-II, or H3K27ac. The reviewer requests clarification on how the authors plot these heatmaps and questions whether the statement is supported by the analysis as presented.

Response: We acknowledge the reviewer’s concern and based on their suggestion, we utilised another set of GRO-seq datasets which is more deeply sequenced and published by the same lab. The average plot from these new datasets showed better profile. We also apologize for not providing enough details of how we generated the heatmaps in Fig. 4B. The heatmaps were made separately for each profile to auto scale with their own intensity levels but the order of the regions is based on KAS-seq intensity. The order of these regions was kept the same between each profile. Hence, top loci of ssDNA are not exact top loci of GRO, ER, H3K27ac and Polymerase but top loci of ssDNA also show similar high intensity in GRO, ER, H3K27ac and Polymerase, hence correlated. We also removed regions which belong to blacklisted regions of hg38 and the regions which were over-sequenced due to amplifications and showed weird signals. We provided the new heatmaps and profile plots in the revised manuscript with different clusters of KAS-seq intensity. We also updated the methods section to clarify how these heatmaps were made.

7. In Fig. S4B and the third plot of 4C, the averaged histogram of ER binding appears in multiple sharp peaks with drastic asymmetric positioning around the enhancer centre, which is highly atypical of most published ER ChIP-seq profiles. Could the authors discuss possible "spatial syntax" or directional patterns of ER binding in relation to eRNA loci and cite any literature showing a similar pattern? Further evidence is required to substantiate these observations, as they are remarkably unique.

Response: The authors agree with the reviewer’s point about asymmetric peaks of ER on the luminal specific eRNA regions. Due to the nature of the average profile plots and the number of regions explored here are so low, the profiles look asymmetrical and different than the published literature. Heatmaps lose their resolution when made on a very low number of regions. The focus of this analysis is to highlight that the ER is not binding to the centre of eRNA loci which is contradictory to the published findings from in vitro studies, but further away on these subtype-specific regions. We don’t have any solid evidence to demonstrate the directional patterns of ER binding related to this data. To avoid any confusion, we removed these average plots but focused on the already existing single gene profiles in Fig. S3 and discussed our interpretations in detail.

Minor comments<br /> 1. When introducing eRNAs, the reviewer recommends mentioning that 1) eRNA levels correlate with enhancer activity and 2) eRNA expression precedes target gene transcription, thus reflecting upstream regulatory events. Relevant references include: Arner, E. et al. Transcribed enhancers lead waves of coordinated transcription in transitioning mammalian cells. Science 347, 1010-1014 (2015); Carullo, N. V. N. et al. Enhancer RNAs predict enhancer-gene regulatory links and are critical for enhancer function in neuronal systems. Nucleic Acids Res. 48, 9550-9570 (2020); Kaikkonen, Minna U. et al. Remodeling of the Enhancer Landscape during Macrophage Activation Is Coupled to Enhancer Transcription. Mol. Cell 51, 310-325 (2013).

Response: These are great recommendations from the reviewer, and we included the suggested publications in the Introduction section of the revised manuscript.

2. H3K27ac is used initially to define these regulatory loci, and like eRNAs, H3K27ac also varies among patients. Which H3K27ac dataset(s) were used initially, and could this approach potentially overlook patient-specific enhancers? (OPTIONAL)

Response: This is a totally valid point from the reviewer. The idea of this project is to define common subtype-specific enhancers which can be regulatory and prognostic, hence can be developed further as biomarkers providing benefit for more patients in the future. Hence, investigating the common enhancers which are activated in multiple normal and cancer cell lines defined by ENCODE is more valid than patient-specific enhancers whose activity might be influenced by specific genetic alterations. There is very limited availability of H3K27ac ChIP-seq datasets from cancer patients to explore the patient-specific enhancers, and our analyses were totally based on the published work, hence not possible to fully address this concern. The source of the H3K27ac ENCODE datasets (from 86 human cell lines and tissue samples) is clarified in the revised manuscript.

3. In addition to the overall metrics displayed in Fig. 2B, could the authors provide precision and sensitivity values for LumA and LumB separately under the Logmc method, given the observation in Fig. 2E that LumA and LumB are not well separated in the UMAP projection?

Response: The authors appreciate the suggestion from the reviewer. We have included the metrics separately for LumA and LumB in the revised manuscript in Fig. S1D.

4. Could the author elaborate, in the discussion section, on why there is a substantial difference in ML performance depending on whether InfoGain or Logmc is used?

Response: We have included the following text in the discussion to explain the differences between these two measures.

“InfoGain measure work with the approach of binarization with k-means (k=2). It has the potential to capture both strongly expressed eRNAs which are differential between subtypes as well as low expressed sparser on and off eRNAs. In the first case, although eRNA is highly expressed in all patients, the higher expression mode becomes 1 and the lower expressed mode become 0. However, in case of low expression, more on and off expression, recentered logmc would not generate a striking high value. Furthermore, binarization is also a strong process to perform better clustering and classification, as distinguishing between data points gets better and clearer. “

5. How does the expression pattern of Basal high, Basal low, Her2, and Lum eRNA clusters behave differentially in Basal, Her2, and LumA/B subtypes? Are Basal high eRNAs downregulated in Her2 or Lum subtypes, and vice versa? Since many downstream analyses rely on these eRNA clusters, it is suggested to include a heatmap and/or boxplot that displays how each eRNA category is expressed in each subtype to confirm that these definitions are consistent.

Response: We thank the reviewers for this suggestion and apologise for not providing enough clarification on the expression of eRNAs in other subtypes. Indeed, Basal high expressed eRNA are expressed low in LumA and LumB and Basal low expressed eRNAs are expressed higher in lumA and lumB. Her2 subtype-specific eRNAs has a trend of expression between Basal and Lum, as it can be seen in the umap and PCA. Basically, the Basal high expressed eRNAs are Lum lower expressed eRNAs, and the Basal low expressed markers are Lum higher expressed markers. As per the suggestion from the reviewer, we provided heatmaps on eRNA expression of each subtype-specific with regulation in other subtype patients in figure S2F-K.

Referee cross-commenting

I share Reviewer #1's opinion that the manuscript should assess whether mRNA or eRNA is the stronger predictor of breast cancer subtypes and clinical outcomes. It will greatly improve the novelty if eRNA is shown to be a better indicator for cancer characterization.

Also, I strongly concur with Reviewer #3 that the current informatics approach is superficial and that several conclusions are contentious. The authors need to resolve the inconsistencies in their ML statistics and the potentially misleading interpretations of the ChIPseq and motif enrichment results.

It is further recommended that, building Reviewer #3's comment, the study integrate eRNA signatures with their proximal genes to address 1) whether genes located near these enhancers are differentially expressed-and correlated with enhancer activity-across cancer subtypes, and 2) whether it provides insights into understanding the enhancer-gene regulatory architecture in a subtype-specific context.

Response: We thank reviewer 2 for cross-commenting on reviewer 1 and 3’s suggestions. Indeed, these are interesting points to cover and will increase the novelty of the study. Based upon these suggestions and discussed earlier for reviewer 1’s comments, we will explore the comparison of mRNAs vs eRNAs as predictor of cancer subtypes and prognosis and the association of genes-eRNAs in cis as discussed in other reviewer’s comments. Our preliminary analyses show a strong association of eRNA and mRNA specific to subtypes and an observable separation on subtypes which were harder to classify markers using eRNAs alone. Hence, we will improve these analyses, and the manuscript further as discussed above in the final revision.

Significance

General Assessment

This study provides insights into the potential use of eRNA to classify breast cancer subtypes and refine prognostic markers. A strength is the integration of large-scale RNA-seq data with machine learning to identify eRNA signatures in biologically-meaningful patient samples, revealing both established and novel TF networks. The study also discovered eRNA clusters that correlate with the survival of patients, thus providing strong clinical implications. However, the ML approach yields several inconsistencies-for instance, unsatisfactory classification results for the Her2 subtype as well as the confused statistical metrics in the results. Furthermore, the ML model struggles to differentiate more nuanced molecular classes (e.g., LumA vs. LumB) and higher-level histological subtypes (e.g., lobular vs. ductal), thus limiting its power to dissect more delicate pathological and molecular mechanisms. Another limitation worth noting of this ML approach is the exclusive use of only polyadenylated eRNAs via RNA-seq, which excludes perhaps the more prominent 2D eRNA expressed in regulatory enhancers. Moreover, certain datasets appear to be of suboptimal quality, leading to assertions that would benefit from additional supporting evidence. Altogether, while the study offers a promising angle on eRNA-based tumor stratification, more robust experimental validations are needed to resolve inconsistencies and clarify the mechanistic underpinnings.

Advance<br /> Conceptually, the study highlights the potential for eRNA-based signatures to capture regulatory variation beyond classical markers. However, the utility of these signatures is constrained by the focus on polyadenylated transcripts alone, likely underrepresenting key enhancer regions, and certain evidence presented in this study is not substantial enough to support some statements. While the work adds an important dimension to the understanding of enhancer biology in breast cancer, the resulting insights are partly hampered by limitations in data coverage and quality.

Audience<br /> The primary audience includes cancer epigenetics, functional genomics, and bioinformatics researchers who are interested in leveraging eRNAs as biomarkers and dissecting complex regulatory networks in breast cancer. Clinically oriented scientists focusing on molecular diagnostics may also find relevance in the authors' approach to stratify subtypes and outcomes. The research is most relevant to a specialized audience within basic and translational cancer genomics, as well as computational biology groups interested in eRNA analysis.

Field of Expertise

I evaluate this manuscript as a researcher specializing in cancer epigenetics, functional genomics, and NGS-based data analysis. Parts of the manuscript touching on clinical outcome measures may require additional review from practicing oncologists.

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

This study aims to classify prognostic and subtype-specific eRNAs in breast cancer, highlighting their potential as biomarkers.<br /> Data was analysed using existing machine learning algorithms,<br /> Data analysis is superficial and it is hard to understand the key significant findings.

This is an important topic and a highly relevant approach to identifying RNA-based biomarkers.<br /> They analyse published RNAseq datasets by focusing on molecular subtype-specific eRNAs, enhancing clinical relevance and thereby addressing the heterogeneity of the cancer type (strength of the study).

Weaknesses include: Most of the findings are purely correlation-based and also based on a reanalysis of published datasets; it would benefit from experimental validation to support their findings. Differential expression analysis of large datasets likely yields some differences in the transcriptome. How significant are these changes?<br /> Does the expression of eRNAs affect the expression of genes in cis? Although this analysis would provide some associated gene expression differences, it can also provide some insights into subtype-specific differences in gene expression programs.<br /> If the authors find experimental validations are not feasible, I recommend validating the eRNA signature in an independent dataset.

Response: We acknowledge the weaknesses noticed by the reviewer from this study about the correlation-based analyses of published datasets. While the TCGA eRNA atlas datasets are reanalysed, these are the high-resolution maps ever published on eRNA expression on cancer patient samples, and our study is the first to establish the subtype specific classification of eRNAs. We believe that the eRNAs are biologically relevant, as they are strongly associated with the subtype-specific pathways and epigenetic regulators. Upon suggestion from the reviewers, we will explore the association of mRNAs and eRNAs in cis to establish further significance and relevance of the eRNAs we identified (discussed earlier in reviewer 1 comments).

We would like to focus on studying the functional relevance of eRNAs as a separate project. In vitro studies to establish the knockdown of eRNAs are not straightforward due to the toxicity and non-specific targeting of the locked nucleic acids approach or Cas13-based RNA targeting. siRNA-based approaches don't target the nuclear eRNAs effectively, even though they were widely used by other labs to target eRNAs. Hence, a lot of effort on optimisations are needed to establish functional validation of our eRNAs, hence not under the scope and time frame of this study/revision. To provide validation and significance using independent datasets, we will explore the association of these factors with the expression of subtype-specific eRNAs further in our final revised manuscript using the tools explained above for reviewer 1 (PEGS and Perturb-seq integration). Integration of our classified eRNAs with the published Perturb-seq validated regions from ER+ and ER- breast cancer cell lines will provide the functional validation of patient-associated classified enhancer/eRNAs. Hence, our study would be the first to demonstrate the validated gene-enhancer regulatory networks from breast cancer patient datasets.

Furthermore, we included the single gene visualisation profiles of independent datasets of ER ChIP-seq from different patients (Ross-Innes et al., 2012), ATAC-seq from TCGA patients (Corces et al., 2018), H3K27ac ChIP-seq datasets from cell lines (Theodorou et al., 2013 and Hickey et al., 2021) and GRO-seq and CAGE data published in MCF7 cells close to the eRNA regions and discussed their overlap with the eRNA regions in the revised manuscript. In the final revision, we will perform further detailed integration of all these profiles. Overall, our study will provide the integratory analysis of various independent epigenetic and functional profiles to validate our classified subtype and survival-specific eRNA regions.

Here are major points; addressing these points in the revised version is important.

From Figure 1B, what eRNAs were identified for LumB using log2MC?

Response: The authors acknowledge the lack of analyses on LumB eRNAs in the original version of the manuscript. In the final revised manuscript after associating with mRNAs, we will provide the heatmaps, pathway analyses and other functional annotations for LumB specific eRNAs.

Page 8 However, sensitivity and F-measure .... It would help to include the metrics for the number of patients in each subtype. The ratio of eRNAs/number of cases in each subtype would inform if the number of eRNAs is an outcome of no. of cases or subgroup-specific.

Response: This is a great suggestion from the reviewer, and we included the number of patients for each subtype in the table in Fig. 1D. We observed that the basal patients are low in number, but we identified more basal eRNAs. Hence, the number of eRNAs identified in subtype-specific manner is not correlated to the number of patients in the cohort.

Page 9 "Altogether, both measurements classify eRNAs efficiently based on subtypes, InfoGain allowed us to distinguish further samples based on high and low expression of eRNAs for basal subtype and performed better in statistical metrics" Based on statistical metrics, both models seem to be performing similarly except for Her2.

Response: We apologise for this wrong interpretation. We corrected this in the revised manuscript at page 9.

In Fig. 1B, the F-measure metrics are wrong for basal LogMC, as it is 0.94 rather than 0.54, which could lead to a misinterpretation of the model.

Response: We apologise for the mistake in this figure, and we included the corrected heatmap in the revised manuscript.

Many genome browser figures, including Figure S3. TFBS is not at the same site as eRNAs detected. Is there CAGE data to show that binding these TFs at these sites leads to the expression of eRNAs? That will give direct evidence that the eRNAs are transcribed due to these TFs

Response: This is a great suggestion from the reviewer. We incorporated ATAC-seq, H3K27ac ChIP-seq, CAGE and GRO-seq data on the gene profiles in Fig. S3 to validate the activity of these ER binding sites in the preliminarily revised manuscript. We observed that all the ER binding sites are accompanied by open and active enhancer marks with bidirectional transcription (either GRO- or CAGE positive) but they are not on the exact location of eRNA regions (250-1000 bps away from the centre of ER binding site). Subtype-specific eRNA regions close to genes like MLPH and XBP1 possess active bidirectional transcribing ER binding sites far away from subtype-specific eRNA loci and also ER unbound sites. However, these distal ER binding sites are close to the regions from the list of 300K eRNA loci and they were simply not identified as subtype-specific regions.

Page 10, There were 30 Her2-specific eRNA regions.... Do the same enhancers also regulate these genes as those from which eRNAs are transcribed? Is it cis-effect, or could these affect the trans-regulating of other genes?

Response: We acknowledge the concern from the reviewer, however this is hard to be validated, as functional experiments to explore the 3D interactions of enhancers and gene promoters are not robust enough to be performed in patient samples and can't be performed within the revision time frame. In the final revised manuscript, we will explore the association of enhancers and promoters of ERBB2 with PEGS association as discussed above and with available HiC datasets in Her2+ cell lines (HCC1954, GSE167150, Kim et al., 2022 https://pubmed.ncbi.nlm.nih.gov/35513575/ )

Minor comments:

Page 8 "InfoGain meausure..." Fig. S2A also shows high and low expressed eRNAs for the basal group

Response: We apologise for the lack of clarity here. InfoGain measure identifies both high and low expressed eRNAs in all patients showing similar pattern of regulation among patients. However, logmc derived eRNAs are highly expressed in most patients. Low expressed eRNAs could not be identified in logmc measure as strong as InfoGain regions. The text in the results had been edited in the revised manuscript to reflect better clarity on this point.

Page 11, Our analyses also identified the role of another..... The statement is misleading as it is the enrichment of these TFs with the eRNAs<br /> Response: We included the word “enrichment” to clarify this statement.

Page 13, "Around 90% of eRNAs are bidirectional and non-polyadenylated [53]. TCGA expression datasets are based on RNA-seq assays, which capture only non-polyadenylated RNAs. Thus, analysing the expression of eRNAs on mRNA-seq datasets might not be adequate". It is very confusing, please check<br /> Response: We apologise for the mistake, and this has been corrected in the revised manuscript.

Reviewer #3 (Significance (Required)):

This is an important topic and a highly relevant approach to identifying RNA-based biomarkers.<br /> They analyse published RNAseq datasets by focusing on molecular subtype-specific eRNAs, enhancing clinical relevance and thereby addressing the heterogeneity of the cancer type (strength of the study).

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Reply to the reviewers

Manuscript number: RC-2025-03004

Corresponding author(s): Kentaro Furukawa and Tomotake Kanki

1. General Statements [optional]

We would like to thank the reviewers for their constructive and positive feedback. We are encouraged that all three reviewers consider the identification of Mfi2 as an outer mitochondrial membrane fission factor required for mitophagy to be a significant and important contribution to the research field. We acknowledge the concerns raised and propose the following plan to address them through additional experiments and clarifications. We believe that these revisions will further strengthen the manuscript and enhance its impact.

2. Description of the planned revisions

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

Furukawa and colleagues identified Mfi2 as novel factor that promotes fragmentation and removal of damaged mitochondria by mitophagy. They report that parallel loss of Dnm1 and Mfi2 blocks mitophagy. Mfi2 acts on the outer membrane, while the previous found Atg44 functions in the intermembrane space. How the proteins cooperate remains unknown. This is an elegant study with high-quality data. The findings are interesting for a broad readership. There are some issues as outline below that should be solved.

Response:

We would like to thank Reviewer #1 for their thoughtful evaluation of our manuscript and for recognizing the interest and quality of the study.

1. It remains unclear how Mfi2 is anchored into the outer mitochondrial membrane. Does it contain a transmembrane domain? The carbonate resistance indicates the presence of such transmembrane domain. However, the presented structures lack such membrane-spanning segment. This point should be clarified.

Response:

We performed an in silico topology prediction of Atg44 and Mfi2 using TMHMM. This tool identified a weakly hydrophobic region of Mfi2 near the N-terminus but did not predict a definitive transmembrane domain (see new Fig. EV1E) (Page 6, lines 8-9). This result implies that Mfi2 interacts with the outer membrane in a monotopic or peripheral manner, rather than as a classical transmembrane protein. Such proteins may remain in the membrane pellet after carbonate treatment due to their strong hydrophobic insertion into the lipid bilayer (e.g., yeast tafazzin/Taz1; Brandner et al., Mol. Biol. Cell, 2005; DOI: 10.1091/mbc.E05-03-0256). We will incorporate this interpretation in the revised manuscript.

How does Mfi2 cooperate with Dnm1? Is there any interaction between these proteins? Some further information could provide mechanistic insights into the function of Mfi2.

Response:

While our study does not explicitly suggest that Mfi2 cooperates with Dnm1, we plan to investigate whether these proteins physically associate. We will perform co-immunoprecipitation experiments under growing and mitophagy-inducing conditions to examine potential interactions between Mfi2 and Dnm1. Further insights into their interaction could help clarify the mechanistic role of Mfi2 in mitochondrial fission and mitophagy.

The authors report a CL-dependent binding of Mfi2 to liposomes. Is the recruitment of Mfi2 to mitochondria impaired when CL-synthesis is blocked, e.g. in crd1delta mitochondria?

Response:

To assess the role of cardiolipin in Mfi2 localization, we will compare the efficiency of mitochondrial targeting of endogenous Mfi2 in WT and crd1Δ cells. Additionally, as mentioned in Reviewer #3's comment, we plan to perform coarse-grained molecular dynamics simulations to further investigate the interaction between Mfi2 and cardiolipin. The results of these simulations will be incorporated into the discussion to provide deeper mechanistic insights.

Figure 4B: a wild-type control should be added.

Response:

We appreciate Reviewer #1’s suggestion to include a WT control in Figure 4B. However, given the focus of this figure on the rescue of mitophagy defects in the mfi2Δ dnm1Δ strain, we believe that adding a WT control is not essential for the analysis. The key comparison here is between the mfi2Δ dnm1Δ strain and the rescue conditions, and statistical analysis was performed to support the conclusions. We hope this clarifies our approach, but we will make adjustments if necessary.

Reviewer #1 (Significance (Required)):

The reported findings are interesting for a broad readership.

Response:

We appreciate Reviewer #1’s recognition of the relevance of our findings to a broad readership.

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

In this study, the authors discover a mitochondrial fission factor, termed Mfi2, that promotes mitophagy efficiency and that functions in a partially redundant way with Dnm1 for the fission of mitochondrial outer membranes during mitophagy. The discovery helps to clarify why Dnm1 does not appear to be essential for fission mediated mitophagy by Dnm1. Mfi2 is structurally similar to the inner membrane fission factor Atg44 which is consistent with Mfi2's fission activity. The authors show that Mfi2 has membrane fission activity towards nanotubes in vitro, and that membrane binding is dependent of high levels of cardiolipin, a mitochondrially enriched lipid. In summary, the authors show that Mfi2 mediates mitochondrial outer membrane fission together with Drp1, whereas Atg44 mediates inner membrane fission, that together are necessary for mitophagy.

Response:

We thank Reviewer #2 for the positive assessment and for clearly summarizing the main contributions of our work.

Major: 1. Figure 2: How do the expression levels of the Mfi2 constructs compare to the endogenous levels of the protein? This will help to gauge to what degree Mfi2 N66 overexpression is needed to achieve mitochondrial fragmentation in Atg44 delta cells and also the low level of mitophagy rescue that was observed.

Response:

We used the TDH3 promoter for the expression of Mfi2 in Figures 2D and 2E. Unfortunately, our Mfi2 antibody only detects full-length Mfi2, as it recognizes a C-terminal region of the protein. This means we cannot directly compare the expression levels of Mfi2(N66) to those of endogenous full-length Mfi2. To clarify the expression levels, we will provide the following data:

(1) Mfi2 antibody: Endogenous Mfi2(Full) and overexpressed Mfi2(Full)

(2) FLAG antibody: Overexpressed Mfi2(Full)-FLAG and overexpressed Mfi2(N66)-FLAG

Figure 3A-B: The cardiolipin binding results in vitro are interesting but the concentration of cardiolipin is much lower on the outer membrane versus the inner membrane. Can the authors comment on whether the cardiolipin levels used on the nanotubes are relevant to that of the mitochondrial outer membrane where Mfi2 is located? Can the authors provide quantitative data for these experiments to help strengthen their conclusions?

Can the authors also use purified MBP alone or a form of Mfi2 that cannot bind to membrane e.g. Mfi2-C33) as a control?

Response:

We thank the reviewer for raising this important point regarding our cardiolipin-dependent in vitro data. In our experiments, we used 20 mol% cardiolipin (CL), a concentration higher than the typical levels in the mitochondrial outer membrane, which contains less than 5% CL. However, it is known that CL translocates to the outer membrane under mitophagy-inducing conditions (e.g., Chu et al., Nat Cell Biol, 2013; Kagan et al., Cell Death Differ, 2016). Our use of elevated CL levels aligns with standard practices in in vitro reconstitution assays to ensure adequate membrane curvature and charge density, which are necessary for robust and reproducible protein-membrane interaction assessments.

To strengthen our conclusions, we will provide a quantitative analysis of the nanotube fission experiments. This will include the percentage of severed tubes under each condition, the total number of tubes analyzed (n), and the relationship between tube diameter and fission efficiency. These additional data will allow for a more thorough evaluation of the membrane fission activity of Mfi2.

Furthermore, we will include control experiments using purified MBP alone and a membrane-binding-deficient mutant of Mfi2 (C33), as suggested by the reviewer.

Figure 4D: The protrusions are very difficult to visualize. Can the authors also provide zoomed in regions. Is the data representative from 3 or more independent experiments? Can the authors provide a graph of the quantitation to aid readers with analysis of the data?

Response:

We thank the reviewer for this helpful suggestion. In the revised manuscript, we will provide higher magnification images to improve the visibility of mitochondrial protrusions. We confirm that the presented images are representative of results obtained from three independent experiments. Additionally, as requested, we will include a graph quantifying the frequency and morphology of protrusions to facilitate data interpretation.

Figure 4D: It is fascinating to see the mitochondrial protrusion formation being dependent on autophagy factors but not mitochondrial fission factors. To help visualize this, can the authors image one of either Atg1, Atg8 to address whether phagophores are forming on the protrusions and if so where they are positionally located on the protrusion in control and/or mfi2,dnm1,atg44 triple mutant cells?

Response:

We thank the reviewer for this insightful comment. In our previous study (Fukuda et al., Mol Cell, 2023), we demonstrated that Atg proteins, such as Atg8, accumulate at mitochondrial protrusions formed in atg44Δ cells, suggesting that these structures can serve as sites for phagophore assembly. However, as in our previous microscopy analysis, the resolution limitations of our imaging system make it difficult to precisely determine the exact location of phagophores on the protrusions.

Whether similar recruitment occurs in the absence of both Mfi2 and Dnm1 remains untested. To address this, we will perform fluorescence imaging of fluorescent protein tagged Atg proteins, such as GFP-Atg8, in mfi2Δ dnm1Δ atg44Δ triple mutant cells to examine whether phagophores form on the mitochondrial protrusions under these conditions. This will help us determine whether phagophore formation requires mitochondrial fission or occurs independently of it.

Minor: 1. Is it possible to target Atg44 to the mitochondrial outer membrane, either by attaching an OM anchor or using part of the N-terminus of Mfi2? This will help elucidate how Mfi2 reaches the outer membrane and whether Atg44 can be just as active on the outer membrane as long as it can access it.

Response:

We thank the reviewer for this suggestion. We will construct chimeric proteins between Atg44 and Mfi2 and examine where such proteins are localized. Additionally, we will assess whether these chimeric proteins have the functional activity of Mfi2, as this will help determine if Atg44 can be active on the mitochondrial outer membrane when properly targeted.

Are microtubules or actin required for the protrusions to form? Using the triple mutant cells that have a high proportion of protrusions, it could be tried to add cytoskeletal depolymerizing drugs such as nocodazole for microtubules or Latrunculin A or Latrunculin B for actin.

Response:

We thank the reviewer for this suggestion. We will test the effect of cytoskeletal depolymerizing drugs on protrusion formation in the mfi2Δ dnm1Δ atg44Δ triple mutant cells.

Reviewer #2 (Significance (Required)):

Significance: The discovery of Mfi2 as an outer membrane mitophagy fission factor is an exciting, and very important and significant contribution to the field. The data are in this study are clear and the conclusions are generally well supported by the experiments. This study appears to be suitable as a report style manuscript given that there is limited mechanistic analysis of Mfi2 activity. This does not affect the importance of the work, it just means that it is suited as a report of a significant discovery. Overall, this fills an important knowledge gap in solving the mystery behind which factors are involved in mitochondrial outer membrane fission during mitophagy, and provides a clarification why Dnm1 loss alone minimally affects mitophagy. This work will appeal to researchers interested in mitochondrial biology, the autophagy field, and cell biologists interested in organelle membrane dynamics, and is also broadly important and interesting to all cell biologists.

Reviewer expertise: mitophagy mechanisms, cell biology of mitophagy, autophagy and autophagosome formation, mitochondrial biology including OXPHOS and mitochondrial dynamics

Response:

We appreciate Reviewer #2’s comments on the importance and potential impact of our discovery for the mitophagy and cell biology fields.

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

The manuscript by Furukawa et al. presents a well-structured and thorough study identifying Mfi2 as a novel mitochondrial outer membrane-resident fission factor required for mitophagy in Saccharomyces cerevisiae. The authors demonstrate that Mfi2, together with the inner membrane mitofissin Atg44 and the dynamin-related GTPase Dnm1, contributes to mitochondrial fragmentation during mitophagy. Importantly, they show that while Dnm1 is dispensable on its own, Mfi2 and Dnm1 act redundantly from the outer membrane to support Atg44-mediated fission. The data are robust, the figures are clear, and the mechanistic insight into how mitophagy-specific fission is achieved is of high relevance to the field of mitochondrial quality control.

Overall, this is a logically constructed and convincing study with important implications for understanding compartment-specific mechanisms of mitochondrial fission during selective autophagy. The conclusions are largely well supported by the data. However, a few issues and points of clarification should be addressed before publication.

Response:

We thank Reviewer #3 for the careful and constructive review and for acknowledging the logical structure and robustness of our data.

Major Comments

1. The observation that both Mfi2 and Atg44 require high cardiolipin (CL) content for membrane binding and fission in vitro is intriguing, especially given that CL is enriched in the inner membrane. The authors mention CL externalisation during mitophagy, but this connection could be made more explicit earlier in the manuscript. Furthermore, since the molecular mechanism of membrane interaction remains unresolved, I would strongly encourage the authors to undertake coarse-grained molecular dynamics simulations to explore how Mfi2 might interact with lipid bilayers of differing composition. This could clarify the role of CL and the potential structural contribution of the disordered C-terminal region. Response:

We thank the reviewer for highlighting the need to clarify the connection between CL externalization and the observed CL-dependent membrane binding and fission activity of Mfi2 and Atg44. While we briefly mentioned CL externalization during mitophagy in the Discussion, we agree that this connection should be made more explicit earlier in the manuscript. In the revised version, we will incorporate a brief rationale in the Results section to clarify that CL translocates to the mitochondrial outer membrane under mitophagy-inducing conditions (e.g., Chu et al., Nat Cell Biol 2013). This will provide a physiological basis for our in vitro reconstitution assays using CL-containing liposomes.

We also appreciate the reviewer’s suggestion to explore the molecular basis of Mfi2-lipid interaction through coarse-grained molecular dynamics (CGMD) simulations. In collaboration with Dr. Yuji Sakai, we will perform coarse-grained molecular dynamics (CGMD) simulations to investigate how Mfi2 interacts with lipid bilayers of varying compositions, focusing particularly on the role of cardiolipin and the structural contribution of the disordered C-terminal region. If successful, we will include the results in the revised manuscript.

While the genetic and phenotypic data indicate that Mfi2 and Dnm1 act independently to support mitochondrial fission, the spatial and temporal organisation of their activity during mitophagy remains unclear. Do Mfi2 and Dnm1 colocalise at fission sites, or do they act at separate subdomains of the outer membrane? Live-cell imaging with fluorescently tagged Mfi2 and Dnm1, particularly during mitophagy induction, could help clarify whether these factors act in concert or at distinct locations and time points. This would also help determine whether their apparent redundancy reflects parallel mechanisms or functional compensation at shared sites. It would also be interesting to combine this with Atg44.

Response:

We thank the reviewer for this insightful comment. We plan to perform co-localization analysis of Mfi2 and Dnm1 during mitophagy induction to clarify whether these proteins colocalize at fission sites or act at separate subdomains of the outer membrane. Additionally, we will conduct co-immunoprecipitation experiments of Mfi2 and Dnm1 (see also Response to Reviewer #1’s major comment 2) to further investigate their potential interaction. It is challenging to analyze Mfi2, Dnm1, Atg44, and mitochondrial fission sites simultaneously, as fluorescence-tagged Atg44 has been shown to lose its function (Fukuda et al., Mol Cell, 2023).

Minor Comments

1. The sodium carbonate extraction and proteinase K assays (Figure 1E-F) are standard but may not be familiar to all readers. A brief explanatory sentence clarifying what these methods reveal about membrane topology would improve accessibility. Response:

We thank the reviewer for this helpful comment. We have added a brief explanatory sentence in the revised manuscript to clarify the principles and interpretation of the sodium carbonate extraction and proteinase K assays (Page 5, lines 23-25; Page 6, lines 1-3).

While immunoblot quantifications are shown throughout, it would be helpful to include statistical analysis where appropriate, especially in cases where differences between genotypes or constructs are modest.

Response:

Statistical analyses have been added for immunoblot quantifications where appropriate, particularly in cases where differences between genotypes or constructs are modest.

The naming of Mfi2 as a mitofissin is consistent with previous terminology introduced for Atg44, but the term remains relatively new. A brief clarification distinguishing "mitofissin" from the better-known "mitofusin" family in mammals would help avoid confusion for readers less familiar with yeast-specific nomenclature.

Response:

We have added a brief explanation of the term "mitofissin" to distinguish it from the mammalian "mitofusin" family in Introduction (Page 3, line 26-Page 4 line 1).

Reviewer #3 (Significance (Required)):

This is a strong and well-executed study that provides mechanistic insight into how mitochondrial fission is coordinated during mitophagy in yeast. A major strength is the identification and characterisation of Mfi2 as a previously unrecognised outer membrane fission factor acting in parallel with Dnm1 and in coordination with the intermembrane space protein Atg44. The genetic, imaging, and in vitro biochemical data are carefully integrated, and the authors are transparent about limitations, including open questions around the C-terminal domain of Mfi2, CL dependence, and the evolutionary conservation of mitofissins.

The work makes a conceptual advance by showing that mitophagy-specific mitochondrial fission requires the cooperation of spatially separated factors acting from both the inside and outside of mitochondria, a mechanism that had not been fully appreciated. This study helps resolve previous contradictions regarding the dispensability of Dnm1 in mitophagy, thereby filling a gap in our understanding of organelle-specific fission. While the findings are focused on yeast, they raise broader questions about whether similar principles apply to higher eukaryotes (historically yeast research was always at the forefront of autophagy field).

The study will be of interest to specialists in autophagy, mitochondrial dynamics, and yeast cell biology, as well as researchers working on membrane remodelling and organelle quality control. While the audience is primarily specialised, the conceptual insights will resonate more broadly in the cell biology community.

I am an expert in mitophagy mechanisms in mammalian cells, and while not a specialist in yeast models, I found the study logical, rigorous, and of clear relevance to the broader autophagy field.

Response:

We are grateful for Reviewer #3’s recognition of the conceptual advance provided by our study and its relevance beyond yeast biology.

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

Responses to Reviewer #1:

・We performed in silico topology prediction of Atg44 and Mfi2 using TMHMM. This tool identified a weakly hydrophobic region of Mfi2 near the N-terminus but did not predict a definitive transmembrane domain (new Fig. EV1E) (Page 6, lines 8-9).

Responses to Reviewer #3:

・We have added a brief explanatory sentence in the revised manuscript to clarify the methods and interpretation of the sodium carbonate extraction and proteinase K assays (Page 5, lines 23-25; Page 6, lines 1-3).

・Statistical analyses have been added for immunoblot quantifications where appropriate, particularly in cases where differences between genotypes or constructs are modest.

・We have added a brief explanation of the term "mitofissin" to distinguish it from the mammalian "mitofusin" family in Introduction (Page 3, line 26-Page 4, line 1).

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

Response to Reviewer #1 (Major 4):

We will not include the WT strain as a control. See our response.

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

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Furukawa et al. presents a well-structured and thorough study identifying Mfi2 as a novel mitochondrial outer membrane-resident fission factor required for mitophagy in Saccharomyces cerevisiae. The authors demonstrate that Mfi2, together with the inner membrane mitofissin Atg44 and the dynamin-related GTPase Dnm1, contributes to mitochondrial fragmentation during mitophagy. Importantly, they show that while Dnm1 is dispensable on its own, Mfi2 and Dnm1 act redundantly from the outer membrane to support Atg44-mediated fission. The data are robust, the figures are clear, and the mechanistic insight into how mitophagy-specific fission is achieved is of high relevance to the field of mitochondrial quality control. Overall, this is a logically constructed and convincing study with important implications for understanding compartment-specific mechanisms of mitochondrial fission during selective autophagy. The conclusions are largely well supported by the data. However, a few issues and points of clarification should be addressed before publication.

Major Comments

1. The observation that both Mfi2 and Atg44 require high cardiolipin (CL) content for membrane binding and fission in vitro is intriguing, especially given that CL is enriched in the inner membrane. The authors mention CL externalisation during mitophagy, but this connection could be made more explicit earlier in the manuscript. Furthermore, since the molecular mechanism of membrane interaction remains unresolved, I would strongly encourage the authors to undertake coarse-grained molecular dynamics simulations to explore how Mfi2 might interact with lipid bilayers of differing composition. This could clarify the role of CL and the potential structural contribution of the disordered C-terminal region.
2. While the genetic and phenotypic data indicate that Mfi2 and Dnm1 act independently to support mitochondrial fission, the spatial and temporal organisation of their activity during mitophagy remains unclear. Do Mfi2 and Dnm1 colocalise at fission sites, or do they act at separate subdomains of the outer membrane? Live-cell imaging with fluorescently tagged Mfi2 and Dnm1, particularly during mitophagy induction, could help clarify whether these factors act in concert or at distinct locations and time points. This would also help determine whether their apparent redundancy reflects parallel mechanisms or functional compensation at shared sites. It would also be interesting to combine this with Atg44.

Minor Comments

1. The sodium carbonate extraction and proteinase K assays (Figure 1E-F) are standard but may not be familiar to all readers. A brief explanatory sentence clarifying what these methods reveal about membrane topology would improve accessibility.
2. While immunoblot quantifications are shown throughout, it would be helpful to include statistical analysis where appropriate, especially in cases where differences between genotypes or constructs are modest.
3. The naming of Mfi2 as a mitofissin is consistent with previous terminology introduced for Atg44, but the term remains relatively new. A brief clarification distinguishing "mitofissin" from the better-known "mitofusin" family in mammals would help avoid confusion for readers less familiar with yeast-specific nomenclature.

Significance

This is a strong and well-executed study that provides mechanistic insight into how mitochondrial fission is coordinated during mitophagy in yeast. A major strength is the identification and characterisation of Mfi2 as a previously unrecognised outer membrane fission factor acting in parallel with Dnm1 and in coordination with the intermembrane space protein Atg44. The genetic, imaging, and in vitro biochemical data are carefully integrated, and the authors are transparent about limitations, including open questions around the C-terminal domain of Mfi2, CL dependence, and the evolutionary conservation of mitofissins.

The work makes a conceptual advance by showing that mitophagy-specific mitochondrial fission requires the cooperation of spatially separated factors acting from both the inside and outside of mitochondria, a mechanism that had not been fully appreciated. This study helps resolve previous contradictions regarding the dispensability of Dnm1 in mitophagy, thereby filling a gap in our understanding of organelle-specific fission. While the findings are focused on yeast, they raise broader questions about whether similar principles apply to higher eukaryotes (historically yeast research was always at the forefront of autophagy field).

The study will be of interest to specialists in autophagy, mitochondrial dynamics, and yeast cell biology, as well as researchers working on membrane remodelling and organelle quality control. While the audience is primarily specialised, the conceptual insights will resonate more broadly in the cell biology community.

I am an expert in mitophagy mechanisms in mammalian cells, and while not a specialist in yeast models, I found the study logical, rigorous, and of clear relevance to the broader autophagy field.

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

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---

Referee #2

Evidence, reproducibility and clarity

In this study, the authors discover a mitochondrial fission factor, termed Mfi2, that promotes mitophagy efficiency and that functions in a partially redundant way with Dnm1 for the fission of mitochondrial outer membranes during mitophagy. The discovery helps to clarify why Dnm1 does not appear to be essential for fission mediated mitophagy by Dnm1. Mfi2 is structurally similar to the inner membrane fission factor Atg44 which is consistent with Mfi2's fission activity. The authors show that Mfi2 has membrane fission activity towards nanotubes in vitro, and that membrane binding is dependent of high levels of cardiolipin, a mitochondrially enriched lipid. In summary, the authors show that Mfi2 mediates mitochondrial outer membrane fission together with Drp1, whereas Atg44 mediates inner membrane fission, that together are necessary for mitophagy.

Major:

1. Figure 2: How do the expression levels of the Mfi2 constructs compare to the endogenous levels of the protein? This will help to gauge to what degree Mfi2 N66 overexpression is needed to achieve mitochondrial fragmentation in Atg44 delta cells and also the low level of mitophagy rescue that was observed.
2. Figure 3A-B: The cardiolipin binding results in vitro are interesting but the concentration of cardiolipin is much lower on the outer membrane versus the inner membrane. Can the authors comment on whether the cardiolipin levels used on the nanotubes are relevant to that of the mitochondrial outer membrane where Mfi2 is located? Can the authors provide quantitative data for these experiments to help strengthen their conclusions? Can the authors also use purified MBP alone or a form of Mfi2 that cannot bind to membrane e.g. Mfi2-C33) as a control?
3. Figure 4D: The protrusions are very difficult to visualize. Can the authors also provide zoomed in regions. Is the data representative from 3 or more independent experiments? Can the authors provide a graph of the quantitation to aid readers with analysis of the data?
4. Figure 4D: It is fascinating to see the mitochondrial protrusion formation being dependent on autophagy factors but not mitochondrial fission factors. To help visualize this, can the authors image one of either Atg1, Atg8 to address whether phagophores are forming on the protrusions and if so where they are positionally located on the protrusion in control and/or mfi2,dnm1,atg44 triple mutant cells?

Minor:

1. Is it possible to target Atg44 to the mitochondrial outer membrane, either by attaching an OM anchor or using part of the N-terminus of Mfi2? This will help elucidate how Mfi2 reaches the outer membrane and whether Atg44 can be just as active on the outer membrane as long as it can access it.
2. Are microtubules or actin required for the protrusions to form? Using the triple mutant cells that have a high proportion of protrusions, it could be tried to add cytoskeletal depolymerizing drugs such as nocodazole for microtubules or Latrunculin A or Latrunculin B for actin.

Significance

The discovery of Mfi2 as an outer membrane mitophagy fission factor is an exciting, and very important and significant contribution to the field. The data are in this study are clear and the conclusions are generally well supported by the experiments. This study appears to be suitable as a report style manuscript given that there is limited mechanistic analysis of Mfi2 activity. This does not affect the importance of the work, it just means that it is suited as a report of a significant discovery. Overall, this fills an important knowledge gap in solving the mystery behind which factors are involved in mitochondrial outer membrane fission during mitophagy, and provides a clarification why Dnm1 loss alone minimally affects mitophagy. This work will appeal to researchers interested in mitochondrial biology, the autophagy field, and cell biologists interested in organelle membrane dynamics, and is also broadly important and interesting to all cell biologists.

Reviewer expertise: mitophagy mechanisms, cell biology of mitophagy, autophagy and autophagosome formation, mitochondrial biology including OXPHOS and mitochondrial dynamics

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

Furukawa and colleagues identified Mfi2 as novel factor that promotes fragmentation and removal of damaged mitochondria by mitophagy. They report that parallel loss of Dnm1 and Mfi2 blocks mitophagy. Mfi2 acts on the outer membrane, while the previous found Atg44 functions in the intermembrane space. How the proteins cooperate remains unknown. This is an elegant study with high-quality data. The findings are interesting for a broad readership. There are some issues as outline below that should be solved.

1. It remains unclear how Mfi2 is anchored into the outer mitochondrial membrane. Does it contain a transmembrane domain? The carbonate resistance indicates the presence of such transmembrane domain. However, the presented structures lack such membrane-spanning segment. This point should be clarified.
2. How does Mfi2 cooperate with Dnm1? Is there any interaction between these proteins? Some further information could provide mechanistic insights into the function of Mfi2.
3. The authors report a CL-dependent binding of Mfi2 to liposomes. Is the recruitment of Mfi2 to mitochondria impaired when CL-synthesis is blocked, e.g. in crd1delta mitochondria?
4. Figure 4B: a wild-type control should be added.

Significance

The reported findings are interesting for a broad readership.

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Reply to the reviewers

Response to Reviewers and Revision Plan

We thank all three reviewers for their thoughtful and constructive comments. We are pleased that the reviewers found our work to be "very interesting," "well written," with "high quality" data that is "convincing" and will be "of broad interest for the community of axon guidance, circuit formation and brain development." We particularly appreciate the recognition that our study provides "novel functions for Cas family genes in forebrain axon organization" and uses "state-of-the art mouse genetics" with "quantitative and statistical rigor." Below are our detailed responses to each reviewer's comments, including extensive additional experiments and analyses that we will perform to significantly strengthen the manuscript.

Reviewer #1

We thank this reviewer for recognizing that our experiments are "carefully done and quantified" with "clear and striking" phenotypes that "support most of the conclusions in the manuscript." We appreciate their acknowledgment that this work will be "of interest to developmental neurobiologists and the axon guidance and adhesion fields."

Major Comments:

__ Authors clearly show that misplaced TCA axons are coordinate with cortical layer defects, with misplaced tbr1+ neurons, in EMX-Cre cas and integrin knockouts, suggesting these axons are following misplaced cells. These results are described as 100% coordinate, but since there is no figure of quantification, authors need to clarify how many embryos were examined for each genotype, as this was not described in results or legends.__ We apologize for this oversight and will provide detailed quantification of this important finding. We examined a total of 11 Emx1Cre;TcKO embryos with 13 controls, and 14 Emx1Cre;Itgb1 embryos with 13 littermate controls at two developmental stages (E16.5 and P0) to quantify the coordination between misplaced Tbr1+ neurons and cortical bundle formation. This quantification will be presented in the main text and figure legend.

Here's a more detailed breakdown of those numbers: For Emx1Cre;TcKO knockouts, we examined 7 controls and 5 mutants at P0, and 6 controls and 6 mutant embryos at E16.5. For the Emx1Cre;Itgb1 knockouts, we examined 5 controls and 6 mutant neonates at P0, and 8 controls and 8 mutant embryos at E16.5.

__ Are the neurons not misplaced in Nex cre cas or integrin knockouts? One would think presumably not, but then what are the tbr1+ cell migration defect caused by? I struggle with the semantics of non-neuronal autonomous role of cas in cortex, since tbr1+ neurons are misplaced, and this is what the axons are mistargeting too. So yes, potentially cas or b1 is not needed in those neurons, but those misplaced neurons are presumably driving the phenotype.__

We agree that this important point requires better explanation. You are absolutely correct that Tbr1+ neurons are not misplaced in NexCre;TcKO mutants (Wong et al., 2023), which is precisely why these animals do not exhibit cortical bundle formation. In addition to our previously published data showing normal location of Tbr1+ neurons in those mutants, we can also provide similar analysis at E16.5 and P0 as a supplemental figure. The model we propose is that Cas genes are required in radial glial cells for proper positioning of deep layer cortical neurons. These correctly positioned neurons, in turn, provide appropriate guidance cues for TCA projections. Hence, our model is that while the role of Cas genes is non-neuronal-autonomous (acting in radial glia rather than in the neurons themselves), the mispositioned Tbr1+ neurons in Emx1Cre;TcKO mutants drive the TCA misprojection phenotype. We will clarify this mechanism in the discussion and provide a new graphical model as a supplemental figure to facilitate conceptualization of our conclusions.

__ Authors need to clarify in the discussion that they can't rule out the cas not also needed in tca neurons, Since neither emx or nex cre would hit those cells.__

We will add the following clarification to the discussion: The analysis of cortical bundle formation in Emx1Cre;TcKOrevealed a comparable phenotype to that observed in NestinCre;TcKO, strongly suggesting a cortical-autonomous role for Cas genes in CB formation. "However, we cannot formally exclude a thalamus-autonomous role for Itgb1 or Cas genes in TCA pathfinding, as we did not ablate these genes exclusively in the thalamus. Future studies using thalamus-specific Cre drivers would be needed to definitively address this question."

__ Could authors add boxes in zoomed out brain images to denote zoom regions. And potentially a schematic demonstrating placement of DiI for lipophilic tracing experiments.__

We will add boxes to denote zoom regions where possible throughout the manuscript. For some high magnification panels, we selected the best representative images, which don't necessarily correspond to specific regions of the lower magnification panels, but we will note this in the figure legends. We will also add a schematic diagram to a supplemental figure illustrating DiI placement for all lipophilic tracing experiments.

Reviewer #2

We thank this reviewer for describing our study as "very interesting," "well written," with data that are "of high quality" and findings that are "convincing." We appreciate their recognition that we used "state-of-the art mouse genetics" and that our work will be "of broad interest for the community of axon guidance, circuit formation and brain development."

Major Comments:

__ Immunofluorescence labeling for other β-integrin family members to examine expression in AC axons may provide insights into why β1-integrin deficiency does not replicate the Cas TcKO phenotype.__ This is an excellent suggestion that we will address experimentally. We will perform RNAscope analysis for integrin β5, β6, and β8 in developing piriform and S1 cortex at E14.5, E16.5, and E18.5, as these are the only other β-integrins expressed during cortical development. We anticipate that this analysis may reveal expression of alternative β-integrins in the neurons that extend axons along the developing anterior commissure, which would provide a potential explanation for why β1-integrin deficiency does not replicate the AC phenotype observed in Cas TcKO animals. These new data will be presented as part of a new figure.

__ Is there any evidence that β1-integrin in developing cortical axons is colocalized with Cas proteins (in vivo or in vitro)?__

We have tested multiple antibodies for p130Cas and CasL without success in cortical tissue. However, we will test two new integrin β1 antibodies and a new p130Cas antibody. While direct colocalization may be challenging due to species restrictions and tissue-specific antibody performance, we will attempt to show regional co-expression in consecutive sections. If the integrin antibodies work, we will present data as a supplemental figure demonstrating that p130Cas (using our BAC-EGFP reporter) and β1-integrin show overlapping expression patterns in developing cortical white matter tracts and neurons, supporting their potential functional interaction. In the end, while we will try to address this critique, we will be limited by the reagents that are available to us.

Minor Comments:

__ How long do the Cas TcKO with the various cre driver survive?__

We have not systematically quantified survival beyond 6 months, but surprisingly, survival up to 6 months of age appears normal for all genotypes examined. This information will be included in the Methods section.

Reviewer #3

We thank this reviewer for acknowledging that our "main claims and conclusions are solidly supported by the data" with "good overall data quality" and "high quantitative and statistical rigor." We appreciate their recognition that we "uncover novel functions for Cas family genes in forebrain axon organization" and that our "overall reporting and discussion of findings is data-driven and refrains from excessive speculation."

Addressing Concerns About Novelty and Impact:

We respectfully disagree with the characterization of our findings as "somewhat incremental." While we acknowledge that similar axonal defects have been described in other lamination mutants, our study makes several novel and significant contributions:

First demonstration of Cas family requirement in forebrain axon tract development: This is the first study to establish roles for Cas proteins in axon guidance, representing a completely new function for these well-studied signaling molecules. Novel β1-integrin-independent role for Cas proteins: Our finding that AC defects occur in Cas mutants but not β1-integrin mutants reveals a previously unknown signaling pathway and challenges the assumption that Cas proteins always function downstream of β1-integrin. Mechanistic insights into cortical-TCA interactions: While the general principle that cortical lamination affects TCA projections has been established, our work provides the first demonstration of how specific adhesion signaling molecules (Cas proteins) control this process through radial glial function. Cell-type specific requirements: Our systematic analysis using multiple Cre drivers provides unprecedented detail about where and when Cas proteins function during brain development, revealing both neuronal-autonomous (AC) and non-neuronal autonomous (TCA) roles.

As Reviewer #2 noted, "The main advancement is a more nuanced understanding of where and when these molecules function during brain development and insights into the origin of the defects observed." This represents significant mechanistic progress in understanding forebrain circuit assembly.

Specific Comments:

Suggestion about cell autonomy testing: We appreciate the optional suggestion to test strict cell autonomy using sparse deletion approaches. While this would indeed be interesting, it would represent a substantial undertaking beyond the scope of the current study. However, we believe our current data using NexCre (which hits early postmitotic neurons) versus NestinCre (CNS-wide deletion) and Emx1Cre (cortical progenitors) provides supportive evidence for neuronal autonomy of the AC phenotype, as mentioned by the reviewer.

In vitro axon guidance assays: This is an excellent suggestion for future molecular studies. In the discussion we identify specific candidate guidance molecules (e.g. Ephrins) that would be prime targets for such experiments.

Cross-Reviewer Comments:

We appreciate Reviewer #3's agreement with the other reviewers' suggestions and will address the quantification of neuronal mispositioning/axon bundle correlation as requested by Reviewer #1.

Additional Improvements:

Beyond addressing the specific reviewer comments, we will make several additional improvements to strengthen the manuscript:

Enhanced statistical analysis: All quantifications will include appropriate statistical tests with clearly stated n values and multiple litters represented. Expanded discussion: We will better contextualize our findings within the broader axon guidance literature and discuss future directions (e.g. TCAs). New data: Additional controls, expression analysis, and quantifications will strengthen our conclusions.

We believe these revisions, particularly the new experimental data addressing integrin family expression and the detailed quantification of phenotype coordination, will significantly strengthen our conclusions and demonstrate the novelty and impact of our findings. We hope the reviewers will find these improvements satisfactory and agree that our work makes important contributions to understanding axon guidance mechanisms in the developing forebrain.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript by Estep et al., the authors use conditional in vivo mouse genetics to study roles for Cas family intracellular adaptor proteins in forebrain axon tract development. They report two phenotypes after simultaneous nervous system-wide deletion of three Cas family genes - (1) defasciculation and misprojection of anterior commissure axons and (2) ectopic formation of thalamocortical axon bundles that penetrate the cortex. Further investigation using specific Cre lines and other conditional knockout alleles demonstrates that the anterior commissure defect results from a requirement for Cas genes in cortical projection neurons, whereas thalamocortical axons are misguided due to Cas functional requirements in cortical lamination, as ectopic axon bundles are confined to sites of disrupted cortical layer formation. Overall, this study uncovers novel functions for Cas family genes in forebrain axon organization, one of which likely reflects a direct role in axon guidance and/or fasciculation, while another one is indirect and based in the previously established role of Integrin-Cas signaling in radial glia organization and cortical neuron migration.

The main claims and conclusions of the paper are solidly supported by the data. The study is fairly descriptive in nature, being limited to in vivo analyses of Cas expression patterns and characterization of the knockout phenotypes, and does not uncover novel molecular mechanisms for axon guidance, but it also does not attempt to make any claims to that effect. The overall reporting and discussion of findings is data-driven and refrains from excessive speculation, which is commendable. The overall data quality is good, and data organization and presentation are clear. Quantitative and statistical rigor are high.

The characterization of Itgb1 knockout animals and various conditional Cas knockouts provides strong evidence that the thalamocortical axon phenotypes are simply a secondary consequence of cortical disorganization, as they strictly segregate with defects in cortical lamination.

The requirement for Cas genes in anterior commissure axon organization is accurately reported as "neuronal-autonomous", but not as cell-autonomous. It would be interesting, yet not essential (i.e. this suggestion is optional), to test for strict cell autonomy by sparsely deleting Cas family genes in a subset of the neurons that project axons through the anterior commissure and analyzing the projection patterns of Cas mutant and control neurons in such a genetic mosaic side by side.

In the discussion, the authors highlight a few of the axon guidance signaling pathways that would be strong candidates for requiring Cas in the context of the anterior commissure. If the authors wanted to develop this idea further, they should consider using in vitro axon guidance assays to study the requirement for Cas function in the axonal response to these candidate guidance molecules.

Referee Cross-commenting

I generally agree to the comments by reviewers 2 and 3. I especially like reviewer 1's suggestion to provide quantitative support for the correlation between sites of neuronal mispositioning and sites of ectopic axon bundle emergence in the cortex. I also agree with that reviewer's idea to box regions in micrographs that are shown in high-magnification panels.

Significance

The strengths of the study lie in its simplicity and limited scope, yet so do its weaknesses. The authors uncover requirements for Cas genes in axon tract organization, but mechanistic insights are extremely limited. On the plus side, the authors refrain from excessive speculation and stay very close to the data in the interpretation and discussion of their findings.

The reported findings are novel, at least to some extent. The same group had previously established the Itgb1-Cas signaling axis as an important regulator of cortical architecture, and results presented here document a thalamocortical axon guidance phenotype that results from defective cortical lamination. Similar axonal defects have been described in other mouse models with lamination phenotypes, and these studies are cited in the manuscript at hand. So while the study is not first to show this interplay between cortical neuronal positioning and thalamocortical axon organization, it does add to the growing body of evidence for this phenomenon. As for the anterior commissure defect, the study is first to establish a role for Cas family genes in development of this axon tract, but beyond evidence that this might be a neuronal-autonomous requirement (but see earlier comment), it does not provide any mechanistic insights into this Cas function. Had the authors identified an actual signaling pathway for axon guidance or bundling that is mediated by Cas proteins and explains their requirement for anterior commissure formation, this study would be a lot more impactful. In its current form, however, the limited genetic and functional insights from this manuscript will largely be of interest to a specialized audience. The overall advance provided by this work is somewhat incremental.

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Referee #2

Evidence, reproducibility and clarity

Summary: In this very interesting study, Estep and colleagues investigate the role of Cas family members (p130Cas, CasL/Nedd9 and Sin/Efs) by generating triple conditional mutant (Cas TcKO) mice to investigate to role in the developing brain (E14.5 - P0), focusing on thalamocortical axons (TCA) and the anterior commissure (AC). For visualization of p130Cas expressing neurons, the p130Cas-EGFP-BAC allele was used. This revealed EGFP (p130Cas) expression in all major cortical tracts and overlap with L1 distribution. Conditional ablation using Nestin-cre (Nes-cre;TcKO) revealed defects in the AC and the external capsule (EC). In addition, these mice show pathfinding defects resulting cortical bundles (CBs) in white matter within the cortical plate. Evidence is provided that these CBs originate from TCA afferents. To assess the cell autonomy of these phenotypes, Emx1-cre;TcKO and Nex-Cre;TcKO mice were generated. Analysis of these mice revealed that Cas genes function in cortical neurons is required for proper TCA development. Nex-cre;TcKO mice only replicated the AC phenotypes observed in Nestin-cre;TcKO mice. Moreover, evidence is provided that proper development of TCA afferents requires non-neuronal functions of Cas genes. Because Cas proteins function downstream of integrins, including beta1-integrin, Itgb1 cKO mice (using Emx-cre or Nex-cre) to examine similarities to Cas TcKO mice. Indeed, Emx-cre;Itgb1 cKO mice phenocopy CB defects observed in the Emx-cre; CasTcKO, while Nex-cre;Itgb1 mutants do not, and neither of the Itgb1 mutants phenocopied the Cas TcKO defects in the AC. Correlative evidence is provided that CBs observed in Cas TcKO mutants originate from disorganization of the subplate.

Overall, this manuscript is well written, and most of the data presented are of high quality. It is also clear that a great deal of effort was put into the experiments, however some issues were identified, and the authors should address them to further clarify and strengthen the work.

Major comments:

1. Immunofluorescence labeling for other b-integrin family members to examine expression in AC axons may provide insights into why b1-integrin deficiency does not replicate the Cas TcKO phenotype.
2. Is there any evidence that b1-integrin in developing cortical axons is colocalized with Cas proteins (in vivo or in vitro)

Minor comments:

1. How long do the Cas TcKO with the various cre driver survive?

Significance

Elucidation of molecular mechanisms of axon pathfinding and brain wiring in vivo. Using state-of-the art mouse genetics; this includes genetic labeling of specific axon tracts, generation of compound mutants in a cell type specific manner and gene products that are thought to function in the same pathway. This was confirmed for some fiber systems, but not for others. The findings presented are convincing and the manuscript is well written. The guidance molecules investigated are not novel and have been analyzed previously, however not with the same rigor or the use of compound mutants. The main advancement is a more nuanced understanding of where and when these molecules function during brain development and insights into the origin of the defects observed. Of broad interest for the community of axon guidance, circuit formation and brain development. I have been studying molecules that regulate axon guidance, growth and regeneration for the past 20+ years.

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Referee #1

Evidence, reproducibility and clarity

In the manuscript by Estep et al., the authors studied Cas proteins expressed during brain development, particularly during the formation of the anterior commissure (AC) and thalamocortical (TCA) projection, using conditional alleles in mice, immunohistochemistry, and a combination of lipophilic axon tracers or genetically encoded fluorophores that mark cells that have expressed Cre. They found that Cas proteins were required for proper guidance of TCA projections and fasciculation of posterior AC axons using broad deletion of Cas gene function by crossing Cas TcKO animals with Nestin-Cre mice- CNS-wide deletions in both neuronal and glial populations, results in axon misprojection and aberrant cortical bundles, of both AC and TCA. With a time course, they find these axon misguidance phenotypes appear at different developmental time points, with AC defasciulation not apparent until e18.5, whereas aberrent TCA Cortical bundles were detected already at e14.5, and increasing over developmental time.

They then go on to use more specific Cre drivers, EMX cre (RGCs, excitatory neurons, mqcroglia in cortex), vs Nex Cre early postmitotic neurons in cortex. EMX cre, still shows TCA defects, even though cas not knocked out of tca axons, suggesting cortical autonomous expression of cas, affects these axons. Because Nex Cre mice didn't show this phenotype, this suggested that the TCA phenotype was cortical-autonomous but not neuronal-autonomous, with mis-projecting TCA processes (cortical bundles) closely associating with misplaced subplate and deep layer neurons. cortical- and neuronal autonomous role for Cas genes during AC fasciculation showed that defasciculating AC axons originated from the dorsolateral cortex. Defects in AC fasciculation were dissimilar to β1-integrin mutants, suggesting that Cas proteins can act independently of β1-integrin during AC formation.

Overall, these data indicate a requirement for Cas family genes during cortical white matter tract formation. The experiments are carefully done and quantified, and the phenotypes are clear and striking, and support most of the conclusions in the manuscript. I only suggest a few points for clarification.

Authors clearly show that misplaced TCA axons are coordinate with cortical layer defects, with misplaced tbr1 + neurons, in EMX-Cre cas and integrin knockouts, suggesting these axons are following misplaced cells. These results are described as 100% coordinate, but since there is no figure of quantification, authors need to clarify how many embryos were examined for each genotype, as this was not described in results or legends.

Are the neurons not misplaced in Nex cre cas or integrin knockouts? One would think presumably not, but then what are the tbr1+ cell migration defect caused by? I struggle a with the semantics of non-neuronal autonomous role of cas in cortex, since tbr1+ neurons are misplaced, and this is what the axons are mistargeting too. So yes, potentially cas or b1 is not needed in those neurons, but those misplaced neurons are presumably driving the phenotype.

Authors need to clarify in the discussion that they can't rule out the cas not also needed in tca neurons, Since neither emx or nex cre would hit those cells.

Could authors add boxes in zoomed out brain images to to denote zoom regions. And potentially a schematic demonstrating placement of DiI for lipophilic tracing experiments.

Significance

The study demonstrates the different requirement for Cas proteins and b1 integrin in different cell populations for appropriate white matter tract formation, and further supports the that cortical layering helps direct TCA projections. It also provides evidence for a b1 integrin independent role for cas proteins. The authors nicely discuss this with several alternative upstream receptors that may be involved detailed, that set the stage for future work, but this would be quite a large endeavor. I would add that it is unclear if cas proteins are needed in the TCA neurons, as they did not use a cre driver that would clarify this. The final limitation I will mention is that EM would likely be required to demonstrate a role for fasiculation, but this also seems beyond this original manuscript. This study will be of interest to developmental neurobiologists and the axon guidance and adhesion fields.

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

In their manuscript de las Mercedes Carro et al investigated the role of Ago proteins during spermatogenesis by producing a triple knockout of Ago 1, 3 and 4. They first describe the pattern of expression of each protein and of Ago2 during the differentiation of male germ cells, then they describe the spermatogenesis phenotype of triple knockout males, study gene deregulation by scRNA seq and identify novel interacting proteins by co-IP mass spectrometry, in particular BRG1/SMARCA4, a chromatin remodeling factor and ATF2 a transcription factor. The main message is that Ago3 and 4 are involved in the regulation of XY gene silencing during meiosis, and also in the control of autosomal gene expression during meiosis. Overall the manuscript is well written, the topic, very interesting and the experiments, well-executed. However, there are some parts of the methodology and data interpretation that are unclear (see below).

Major comments

1= Please clarify how the triple KO was obtained, and if it is constitutive or specific to the male germline. In the result section a Cre (which cre?) is mentioned but it is not mentioned in the M&M. On Figure S1, a MICER VECTOR is shown instead of a deletion, but nothing is explained in the text nor legend. Could the authors provide more details in the results section as well as in the M&M ? This is essential to fully interpret the results obtained for this KO line, and to compare its phenotype to other lines (such as lines 184-9 Comparison of triple KO phenotype with that of Ago4 KO). Also, if it is a constitutive KO, the authors should mention if they observed other phenotypes in triple KO mice since AGO proteins are not only expressed in the male germline.

Response: We apologize for omitting this vital information. We have now incorporated a more detailed description of how the Ago413 mutant was created in the results and M&M sections (line 120 and 686 respectively).

As mentioned in the manuscript, Ago4, Ago1 and Ago3 are widely expressed in mammalian somatic tissues. Mutations or deletions of these genes does not disrupt development; however, there is limited research on the impact of these mutations in mammalian models in vivo. In humans, mutations in Ago1 and Ago3 genes are associated with neurological disorders, autism and intellectual disability (Tokita, M.J.,et al. 2015- doi: 10.1038/ejhg.2014.202., Sakaguchi et al. 2019- doi: 10.1016/j.ejmg.2018.09.004, Schalk et al 2021- doi: 10.1136/jmedgenet-2021-107751). In mouse, global deletion of Ago1 and Ago3 simultaneously was shown to increase mice susceptibility to influenza virus through impaired inflammation responses (Van Stry et al 2012- doi.org/10.1128/jvi.05303-11). Studies performed in female Ago413 mutants (the same mutant line used herein) have shown that knockout mice present postnatal growth retardation with elevated circulating leukocytes (Guidi et al 2023- doi: 10.1016/j.celrep.2023.113515). Other studies of double conditional knockout of Ago1 and Ago3 in the skin associated the loss of these Argonautes with decreased weight of the offspring and severe skin morphogenesis defects (Wang et al 2012- doi: 10.1101/gad.182758.111). In our study, we did not observe major somatic or overt behavioral phenotypes, and we did not observe statistical differences in body weights of null males compared to WT as shown in figure below.

2= The paragraph corresponding to G2/M analysis is unclear to me. Why was this analysis performed? What does the heatmap show in Figure S4? What is G2/M score? (Fig 2D). Lines 219-220, do the authors mean that Pachytene cells are in a cell phase equivalent to G2/M? All this paragraph and associated figures require more explanation to clarify the method and interpretation.

__Response: __We have modified the methods to include more information about how the cell cycle scoring used in Figures 2D and S4 were calculated and will add more information regarding the interpretation of these figures.

3= I have concerns regarding Fig2G: to be convincing the analysis needs to be performed on several replicates, and, it is essential to compare tubules of the same stage - which does not seem to be the case. This does not appear to be the case. Besides, co (immunofluorescent) staining with markers of different cell types should be shown to demonstrate the earlier expression of some markers and their colocalization with markers of the earlier stages.

__Response: __We agree with the Reviewer. New images with staged tubules will be added to the analysis of Figure 2G.

4= one important question that I think the authors should discuss regarding their scRNAseq: clusters are defined using well characterized markers. But Ago triple KO appears to alter the timing of expression of genes... could this deregulation affects the interperetation of scRNAseq clusters and results?

__Response: __We thank the reviewer for this suggestion and agree that including this information is important. We expect that, at most, this dysregulation impacts the edges of these clusters slightly. Given that marker genes that have been used to define cell types in these data are consistently expressed between the knockout and wildtype mice (see Figure S4A), we do not think that the cells in these clusters have different identities, just dysregulated expression programs. We have added the relevant sentence to the discussion, and will include additional supplemental figure panels to document this point more comprehensively.

5= XY gene deregulation is mentioned throughout the result section but only X chromosome genes seem to have been investigated.... Even the gene content of the Y is highly repetitive, it would be very interesting to show the level of expression of Y single copy and Y multicopy genes in a figure 3 panel.

__Response: __We agree with the reviewer that including analysis of Y-linked genes is important. We will add a supplemental figure which includes the Y:Autosome ratio and differential expression analysis.

6= Can the authors elaborate on the observation that X gene upregulation is visible in the KO before MSCI; that is in lept/zygotene clusters (and in spermatogonia, if the difference visible in 3A is significant?)

Response: We do see that X gene expression is upregulated before pachynema. Previous scRNA-seq studies that have looked at MCSI have seen that silencing of genes on the X and Y chromosomes starts before the cell clusters that are defined as pachynema, though silencing is not fully completed until pachynema. We have clarified this point in the manuscript.

7 = miRNA analysis: could the authors indicate if X encoded miRNA were identified and found deregulated? Because Ago4 has been shown to lead to a downregulation of miRNA, among which many X encoded. It is therefore puzzling to see that the triple KO does not recapitulate this observation. Were the analyses performed differently in the present study and in Ago4 KO study?

__Response: __The analysis identifying downregulation of miRNA in the original Ago4 mutant analysis was conducted relative to total small RNA expression. Amongst those altered miRNA families in the Ago4 mutants, we demonstrated both upregulation and downregulation of miRNA. We agree that confirming a similar global downregulation of miRNA counts compared to other small RNAs is important. Therefore, in a revised manuscript, we will add this information to the miRNA analysis section, especially highlighting the X chromosome-associated miRNAs, as well as whether the ratios between other small RNA classes change.

8 = The last results paragraph would also benefit from some additional information. It is not clear why the authors focused on enhancers and did not investigate promoters (or maybe they were but it's unclear). Which regions (size and location from TSS) were investigated for motif enrichment analyses? To what correspond the "transcriptional regulatory regions previously identified using dREG" mentioned in the M&M? I understand it's based on a previous article, but more info in the present manuscript would be useful.

Response: We thank the reviewer for this suggestion. The regions that were used for motif enrichment will be included as a supplementary information in the fully revised manuscript. We have also clarified in the methods that these transcriptional regulatory regions were downloaded from GEO and obtained from previous ChRO-seq data (from GEO) analysis. These data are run through the dREG pipeline that identifies regions predicted to contain transcription start sites, which include promoters and enhancers.

Minor comments

1) In the introduction: The sentence "Ago1 is not expressed in the germline from the spermatogonia stage onwards allowing us to use this model to study the roles of Ago4 and Ago3 in spermatogenesis." is misleading because Ago1 is expressed at least in spermatogonia; It would be more precise to write "after spermatogonia stage" and rephrase the sentence. Otherwise it is surprising to see AGO1 protein in testis lysate and it is not in line with the scRNA seq shown in figure 2.

__Response: __We agree with the Reviewers suggestion and have edited the sentence on line 100. This sentence now reads "Ago1 is not expressed in the germline after the spermatogonia stage allowing us to use this model to study the roles of Ago4 and Ago3 in spermatogenesis".

2) Could the authors precise if AGO proteins are expressed in other tissues? In somatic testicular cells?

__Response: __Expression patterns of mammalian AGOs have been described in somatic and testicular tissues for the mouse by Gonzales-Gonzales et al (2008) by qPCR. They found that Ago2 is expressed in all the somatic tissues analyzed (brain, spleen, heart, muscle and lung) as well as the testis, with the highest expression in brain and lowest in heart. Ago1 is highly expressed in spleen compared to all the tissues analyzed, while Ago3 and Ago4 showed highest expression in testis and brain. Within somatic tissues of the testis, the four argonautes are expressed in Sertoli cells, however, Ago1,3 and 4 expression is very low compared to Ago2, with the latter showing a 10-fold higher transcript level. We have included a sentence with this information in the introduction in line 89.

3) Pattern of expression: How do the authors explain that AGO3 disappears at the diplotene stage and reappears in spermatids?

__Response: __ Single cell RNAseq data in the germline shows reduced transcript for Ago3 from the Pachytene stage onwards, suggesting minimal if any new transcription in round spermatids. We hypothesize that the AGO3 protein present in the round spermatid stage is cytoplasmic, presumably coming from the pool of AGO3 in the chromatoid body, a cytoplasmic structure with functional association with the nucleus in round spermatids (Kotaja et al, 2003 doi: 10.1073/pnas.05093331).

4) It would be useful to show the timing of expression of AGO 1 to 4 throughout spermatogenesis in the first paragraph of the article. Maybe the authors could present data from fig2B earlier?

Response: We understand the Reviewers concern, however, given that Ago expression throughout spermatogenesis was obtained from scRNA seq, we consider that this data should be presented after introducing the Ago413 knockout and the scRNA seq experiment. As Ago1-4 expression was also described in an earlier manuscript by Gonzales-Gonzales et al in the mouse male germline, and our data aligns with this report, we included a sentence about these previous findings in the earlier results section.

5) Line 190: please modify the sentence "reveal no differences in cellular architecture of the seminiferous tubules when compared to wild-type males" to " reveal no gross differences..." since even without quantification of the different cell types it is visible that KO seminiferous tubules are different from WT tubules.

__Response: __We agree with the reviewer, and we modified line 190 (now 173) as suggested. Grossly, seminiferous tubules from Ago413 null males contain the same cell types as in wild type tubules, including spermatozoa. However, our studies show that the number and quality of germ cells is compromised in knockouts, as shown by sperm counts and TUNEL staining.

6) TUNEL analysis: please stage the tubules to determine the stage(s) at which apoptosis is the most predominant.

__Response: __We have complied with the reviewer suggestion. Figure 1G now shows staged seminiferous tubules, and we have replaced the wild type image for one where the staged tubules match the knockout image.

7) Figure S4B does not show an increase of cells at Pachytene stage but at Lepto/zygotene stage (as well as an increase of spermatogonia). Please comment this discrepancy with results shown in Fig2.

__Response: __Figures 2 and S4 show distribution of cells in different substages of spermatogenesis and prophase I measured with very different methods: a cytological approach using chromosome spreads cells vs a transcriptomic approach that involves clustering of cells. We attribute the differences in cell type distribution to differences in the sensitivity of the methods to identify each cell type and therefore identify differences between the number of cells for each group. Moreover, our scRNA-seq data groups the leptotene and zygotene stages together, while the cytological approach allows for separation of these two sub-stages. Importantly, both results show that Ago413 spermatocytes are progressing slower from pachynema into diplonema and/or are dying after pachynema, as stated in line 194 in our manuscript.

8) Fig5H and 5I are not mentioned in the result section. Also, it would be useful to label them with "all chromosomes" and "XY" to differentiate them easily

__Response: __We apologize for the omission and have now cited Figures 5H and 5I in the manuscript (line 453). We have added the suggested labels.

9) Line 530 "data provide further evidence for a functional association between AGO-dependent small RNAs and heterochromatin formation, maintenance and/or silencing." Please rephrase, the present article does not really show that AGO nuclear role depends on small RNAs.

__Response____: __We agree with the reviewer that these data do not directly show a dependence on small RNAs. As our identified localization of AGO proteins to the pericentric heterochromatin coincides with localization of DICER shown previously by Yadav and collaborators (2020, doi: 10.1093/nar/gkaa460), we do believe that our data further implicates small RNAs in the silencing of heterochromatin. Yadav et al shows that DICER localizes to pericentromeric heterochromatin and processes major satellite transcripts into small RNAs in mouse spermatocytes, and cKO germ cells have reduced localization of SUV39H2 and H3K9me3 to the pericentromeric heterochromatin. Given the colocalization of both small RNA producing machinery and AGOs at pericentromeric heterochromatin, the AGOs may bind these small RNAs, and the statement in line 530 refers to how our results provide evidence for the involvement of other RNAi machinery in the silencing of pericentromeric heterochromatin investigated by Yadav et al which likely includes small RNAs.

To clarify this point, we have modified the text accordingly.

10) Line 1256: replace "cite here " by appropriate reference

__Response: __The reference was added to line 1256.

11) Please use SMARCA4 instead of BRG1 name as it is its official name.

__Response: __We have replaced BRG1 with SMARCA4 in the text and figures.

Figures:

Figure 1: Are the pictures shown for Ago3-tagged and floxed from the same stages ? The leptotene stage in 1A looks like a zygotene, while some pachytene/diplotene stage pictures do not look alike.

__Response: __New representative images have been added to figure 1 to match the same substages across the figure.

Figure 1D, please label the Y scale properly (testis weight related to body weight)

__Response: __We have fixed this.

FigS1: Please comment the presence of non-specific bands in the figure legend

__Response: __We have added a sentence in Figure S1 Legend.

Fig 2E and F, please indicate on the figure (in addition to its legend), what are the X and Y axes respectively to facilitate its reading.

__Response: __X and Y axes are now labelled in Figure 2E and F.

2F: please use an easier abbreviation for Spermatocyte than Sp (which could spermatogonia, sperm etc..) such as Scyte I ? (same comment for Fig 3C)

Response: The abbreviation for spermatocyte was changed from Sp to Scyte I in Figures 2 and 3.

Overall, for all figures showing GSEA analyses, could the authors explain what a High positive NES and a High negative NES mean in the results section?

Response: Thank you for this suggestion. We have added this information where the GSEA score of the cell markers is initially introduced.

Significance

Ago proteins are known for their roles in post transcriptional gene regulation via small RNA mediated cleavage of mRNA, which takes places in the cytoplasm. Some Ago proteins have been shown to be also located in the nucleus suggesting other non-canonical roles. It is the case of Ago4 which has been shown to localize to the transcriptionally silenced sex chromosomes (called sex body) of the spermatocyte nucleus, where it contributes to regulate their silencing (Modzelewski et al 2012). Interestingly, Ago4 knockout leads to Ago3 upregulation, including on the sex body indicating that Ago3 and Ago4 are involved in the same nuclear process. In their manuscript, de las Mercedes Carro et al., investigate the consequences of loss of both Ago3 and Ago4 in the male germline by the production of a triple knockout of Ago1, 3 and 4 in the mouse. With this model, the authors describe the role of Ago3 and Ago4 during spermatogenesis and show that they are involved in sex chromosome gene repression in spermatocytes and in round spermatids, as well as in the control of autosomal meiotic gene expression. Triple KO males have impaired meiosis and spermiogenesis, with fewer and abnormal spermatozoa resulting in reduced fertility. Since Ago1 male germline expression is restricted to pre-meiotic germ cells, it is not expected to contribute to the meiotic and postmeiotic phenotypes observed in the triple KO. The strengths of the study are i) the thorough analyses of mRNA expression at the single cell level, and in purified spermatocytes and spermatids (bulk RNAseq), ii) the identification of novel nuclear partners of AGO3/4 relevant for their described nuclear role: ATF2, which they show to also co-localize with the sex body, and BRG1/SMARCA4, a SWI/SNF chromatin remodeler. The main limitation of the study is the lack of information in the method regarding the production of the triple KO, as well as some aspects of the transcriptome and motif analyses. It is also surprising to see that the triple KO does not recapitulate the miRNA deregulation observed in Ago4 KO. The characterization of a non-canonical role of AGO3/4 in male germ cells will certainly influence researchers of the field, and also interest a broader audience studying Argonaute proteins and gene regulation at transcriptional and posttranscriptional levels.

Reviewer #2

Evidence, reproducibility and clarity

In the manuscript titled "Argonaute proteins regulate the timing of the spermatogenic transcriptional program" by Carro et al., the authors present their findings on how Argonaute proteins regulate spermatogenic development. They utilize a mouse model featuring a deletion of the gene cluster on chromosome 4 that contains Ago1, Ago3, and Ago4 to investigate the cumulative roles of AGO3 and AGO4 in spermatogenic cells. The authors characterize the distribution of AGO proteins and their effects on key meiotic milestones such as synapsis, recombination, meiotic transcriptional regulation, and meiotic sex chromosome inactivation (MSCI). They analyze stage-specific transcriptomes in spermatogenic cells using single-cell and bulk RNA sequencing and determine the interactome of AGO3 and AGO4 through mass spectrometry to examine how AGO proteins may regulate gene expression in these cells during meiotic and post-meiotic development. The authors conclude that both AGO3 and AGO4 are essential for regulating the overall gene expression program in spermatogenic cells and specifically modulate MSCI to repress sex-linked genes in pachytene spermatocytes, which may be partially mediated by the proper distribution of DNA damage repair factors. Additionally, AGO3 is suggested to interact with the chromatin remodeler SWI/SNF factor BRG1, facilitating its removal from the sex-chromatin to enable the repression of sex-linked genes during MSCI.

Major Comments: 1. The study utilized a triple knockout mouse model to determine the effect of AGO3 on spermatogenesis, following up on their previous report about the role of AGO4 in spermatogenesis, which resulted from an upregulation of AGO3 in Ago4-/- spermatocytes. However, the results are more difficult to interpret and ascertain the role of AGO3 in these cells, given the absence of any observable phenotype from Ago3 interruption. AGO4 regulates sex body formation, meiotic sex chromosome inactivation (MSCI), and miRNA production in spermatocytes, all of which were noted in the absence of both AGO3 and AGO4, with only an increased incidence of cells containing abnormal RNAPII at the sex chromosomes. It will be necessary to characterize how AGO3 regulates spermatogenic development, including meiotic progression and the regulation of the meiotic transcriptome, and compare these findings with the current observations to determine if the proposed mechanism involving AGO3, BRG1, and possibly AP2 is relevant in this context.

__Response: __While we agree with Reviewer that a single Ago3 knockout will help understand distinct roles of AGO3 and AGO4 in spermatogenesis, the time and resources required to generate a new mouse model are substantial. The analysis included in this current manuscript has already taken over seven years, and with the lengthy production of a new single mutant mouse, validation of the new mouse, and then final analysis, we would be looking at another 3-5 years of analysis. In the current funding climate, and with strong concerns over ensuring reduction in utilization of laboratory mice, we consider this request to be far in excess of what is required to move this important story forward.

The Ago413-/- mouse model has allowed us to associate a nuclear role of Argonaute proteins with a strong reproductive phenotype in the mouse germline. Given the redundancy between Ago3 and Ago4, it is likely that a single Ago3 knockout would have a mild phenotype just like the Ago4 KO. All this said, we agree with the reviewer that analysis of an Ago3 knockout mouse is a valuable next step, just not within this chapter of the story.

1. Does Ago413-/- mice recapitulate the early meiotic entry phenotype observed in Ago4-/- mice? If not, could it be possible that AGO3 promotes meiotic entry, given its strong mRNA expression in spermatogonia according to the scRNAseq data (Fig. 2B)

Response: Our scRNA-seq data shows strong expression of Ago3 in spermatogonia, as mentioned by the Reviewer. Analysis of cell cycle marker expression also shows that the transcriptomic profile of spermatogonia is altered, with higher levels of transcripts corresponding to the later G2/M stages (Figure 2D). Moreover, Ago413 knockouts present an increase in the number of spermatogonial stem cells (Supplementary Figure S4B). However, this cluster represents a pool of quiescent and mitotically active cells entering meiosis, therefore interpretation of these data might be challenging. While specific experiments could be conducted to answer this question, this is outside of the scope of our manuscript. The manuscript as it stands is already rather large, and a full analysis of meiotic entry dynamics would dilute the core message relating to chromatin regulation in the sex body.

1. The authors suggested that the removal of BRG1 by AGO3 is necessary during sex body formation and the eventual establishment of MSCI. However, the BAF complex subunit ARID1A has been shown to facilitate MSCI by regulating promoter accessibility. It will be interesting to determine how BRG1 distribution changes across the genome in the absence of AGO proteins and how that correlates with alterations in sex-linked gene expression.

__Response: __We agree that changes in BRG1 distribution across the genome would be very interesting to identify. However, in this work we show that BRG1/SMARCA4 protein changes its localization in the sex body very rapidly between early to late pachynema. These two substages are only discernable by immunofluorescence using synaptonemal complex markers, as there are currently no available techniques to enrich for these subfractions. Therefore, study of genome occupancy of BRG1 in these specific substages by techniques such as CUT&Tag are not currently possible. However, we are currently working on new methods to distinguish these cell populations and hope eventually to use these purification strategies to perform the studies suggested by this reviewer. Alternatively, the hope is that single cell CUT&Tag methods will become more reliable, and will enable us to address these questions. Both of these options are not currently available to us. The studies by Menon et al (2024-doi:10.7554/eLife.88024.5) provide strong evidence to support that ARID1A is needed to reduce promoter accessibility of XY silenced genes in prophase I through modulation of H3.3 distribution. However, this mechanism and our identification of the removal of BRG1 between early and late pachytema are not inconsistent with one another, as either SMARCA4 or SMARCA2 can associate with ARID1A as part of the cBAF complex, and ARID1A is also not in all forms of the BAF complex which BRG1 are in. The difference between our results and those seen in Menon et al likely indicate that there are multiple forms of the BAF complex which are differentially regulated during MSCI and play different roles in silencing transcription. Further studies of specific BAF subunits are needed to elucidate how different flavors of the BAF complex act at specific genomic locations and meiotic time points.

1. The observations presented in this manuscript (Fig. 1D, 2C, 3D, and 4) suggest a haploinsufficiency of the deleted locus in spermatogenic development. How does this compare with the ablation of either Ago3 or Ago4? Please explain.

Response: Our previous studies in single Ago4 knockouts did not present a heterozygous phenotype (Modzelewski et al 2012, doi: 10.1016/j.devcel.2012.07.003, data not shown). Triple Ago413 knockouts show a much stronger fertility phenotype than single Ago4 knockout. Testis weight of Ago413 homozygous null present a 30% reduction while heterozygous mice show a 15% reduction (Figure 1D), comparable to the 13% reduction previously observed in Ago4-/- males. Sperm counts of Ago413 null and heterozygous males are reduced by 60% and 39% compared to wild type (Figure 1E), respectively, whereas Ago4 null mice have a milder phenotype, with only a 22% reduction in sperm counts. At the MSCI level, both homozygous and heterozygous Ago413 mutant spermatocytes show a similar increase in pachytene spermatocytes with increased RNA pol II ingression into the sex body with respect to wild-type of 35% and 30%, respectively. Ago4 single knockouts show an almost 18% increase in Pol II ingression when compared to wild type. These comparisons are now included in our manuscript in lines 170, 172 and 288. A milder phenotype of the Ago4 knockout and haploinsufficiency in triple Ago413 knockouts but not in Ago4 single knockouts is likely a consequence of the overlapping functions of Ago3 and Ago4 in mammals (and/or overexpression of Ago3 in Ago4 knockouts). In the context of their role in RISC, Wang et al (doi: 10.1101/gad.182758.111) studied the effects of single and double conditional knockouts for Ago1 and Ago2 in miRNA-mediated silencing. They discovered that the interaction between miRNAs and AGOs is highly correlated with the abundance of each AGO protein, and only double knockouts presented an observable phenotype.

Minor Comments: Based on the interactome analysis, it was argued that AGO3 and AGO4 may function separately. Please discuss how AGO3 might compensate for AGO4 (Line 109).

Response: We hypothesize that the combined function of AGO3 and AGO4 is needed for proper sex chromosome inactivation during meiosis. We base this hypothesis on the facts that (i) both proteins localize to the sex body in pachytene spermatocytes, (ii) loss of Ago4 leads to upregulation of Ago3, and (iii) the MSCI phenotype of Ago413 knockout mice is much stronger than the single Ago4 knockout (see above). However, AGO3 and AGO4 might not induce silencing through the same mechanism or pathway. In this work, we observed that their temporal expression in prophase I is different; while AGO3 protein seems to disappear by the diplotene stage, AGO4 is present in the sex body of these cells. Moreover, the proteomic analysis revealed a very low number of common interactors, an observation which could support the idea of AGO3 and AGO4 acting by different (albeit perhaps related) mechanisms to achieve MSCI. It is also possible that common interactors were not identified in our proteomic analysis due to the low abundance of AGO3 and AGO4 in the germ cells, limiting the resolution of the proteomics analysis (note that in order to visualize AGO proteins in WB experiments, at least 60 μg of enriched germ cell lysate must be loaded per lane). Moreover, given the difficulty in obtaining enough isolated pachytene and diplotene spermatocytes to perform immunoprecipitation experiments, we performed IP experiments in whole germ cell lysates, which limits the interpretation of our analysis. If AGO3 and AGO4 protein interactors overlap, then AGO3 would directly substitute for AGO4 leading to silencing in single Ago4 knockouts. However, if AGO3 and AGO4 work together through different, complementary mechanisms, then Ago4 mutant mice likely compensates loss of Ago4 by upregulation of Ago3along with specific interactors of the given pathway. We have added a sentence addressing this matter in line 411 of the results section and lines 506 and 513 of the discussion in the revised manuscript.

In Line 221, it is unclear what is meant by 'cell cycle transcripts'. Does this refer to meiotic transcripts? It is also important to discuss the relevance of the G2/M cell cycle marker genes at later stages of meiotic prophase.

Response: Thank you for this suggestion. We have changed the relevant text to remove redundancies and include more information. We agree that considering the importance of these genes across meiotic prophase is needed, as cells which are in the dividing stage will already have produced the proteins necessary for division. These cells likely correspond to the diplotene/M cluster cells that have a lower G2/M score, potentially causing the bimodal distribution seen in Figure 2D. We have added a sentence addressing this to the manuscript.

While identified as a common interactor of both AGO3 and AGO4 in lines 440-445, HNRNPD is not listed among AGO4 interactors in Table S6. Please correct or explain this discrepancy.

Response: HNRPD was originally identified as an AGO4 interactor using a less strict criteria than the one used in our manuscript: we required consistent enrichment in at least two rounds of IP MS experiments. This reference to HNRNPD was a mistake, given that HNRPD was only enriched in one of our three replicates. Thus, we apologize and have removed the sentence in lines 440-445.

It is unclear whether wild-type cell lysate or lysate containing FLAG-tagged AGO3 was used for BRG1 immunoprecipitation, and which antibody was used to detect AGO3 in the BRG1 IP sample. A co-IP experiment demonstrating interaction between BRG1 and wild-type AGO3 would be ideal in this context. Furthermore, co-localization by IF would be beneficial to determine the subcellular localization and the cell stages the interaction may be occurring. Additionally, co-IP and Western blot methodologies should be included in the methods section.

__Response: __MYC-FLAG tagged AGO3 protein lysates were used for BRG1 Co-Immunoprecipitation, along with an anti MYC antibody to detect AGO3. This is now detailed in the Methods section of our revised manuscript (line 1133).

Regarding BRG1 and AGO3 colocalization by IF, we can confidently show that both AGO3 and BRG1 localize to the sex chromosomes in early pachynema by comparing BRG1/SYCP3 and FLAG-AGO3/SYCP3 stained spreads. We were not able to show colocalization simultaneously on the same cells, given the lack of appropriate antibodies. Our anti FLAG antibody is raised in mouse, while anti BRG1 is raised in rabbit, therefore a non-rabbit, non-mouse anti SYCP3 would be needed to identify prophase I substages, and our lab does not possess such a validated antibody. However, we now have access to a multiplexing kit that allows to use same-species antibodies for immunofluorescence and we can perform these experiments for a revised manuscript.

__Response: __The methods section now includes description of co-IP methodologies (line 1132). Western Blot methodologies are explained in lane 718, under the "Immunoblotting" title.

In line 599, it is unclear what is meant by 'persistence of sex chromosome de-repression'. Please correct or clarify this.

Response: This sentence has been changed and reads: "The persistence of sex chromosome gene expression".

If possible, please add an illustration to summarize the findings together.

Response: We thank the reviewer for this suggestion, and have now added this in Figure 6

Significance

Overall, this study enhances the understanding of gene expression regulation by AGO proteins during spermatogenesis. Several approaches, including functional, histological, and molecular characterization of the triple knockout phenotype, were instrumental in elucidating the role of AGO proteins in MSCI and meiotic as well as postmeiotic gene regulation. The main limitation of the study is that it is challenging to appreciate the role of AGO3 in addition to the previously published role of AGO4 without the inclusion of necessary control groups. Furthermore, the mechanism of action for AGO proteins in meiotic gene regulation was left relatively unexplored. This study presents new findings that will be significant for the research community interested in gene regulation, chromatin biology, and reproductive biology with the above suggestions considered.

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

The authors characterize a CRISPR-Cas9 mouse mutant that targets 3 genes that encode AGO family proteins, 2 of which are expressed during spermatogenesis (AGO3 and AGO4) and one that is said is not expressed, AGO1. This mouse mutant showed that AGO3 and AGO4 both contribute to spermatogenesis success as the "Ago413" mutation gave rise to an additive reduction in testis weight, due to spermatocyte apoptosis, and reduction in sperm count. Furthermore, they use insertion mouse mutants for Ago3 and Ago2 that express tagged versions of their corresponding proteins, which they use in combination with pan-AGO antibodies and Ago mutants to show differential expression and localization properties of AGO2, AGO3, and AGO4 (and the absence of AGO1) during spermatogenesis with a particular focus on meiotic prophase. They perform single-cell RNAseq and intricate analyses to demonstrate a change in distribution of meiotic stages in Ago413 mutants, and the overall cell cycle in spermatogonia and spermatocytes is altered. This analysis shows that the mutation leads to an inability to downregulate prior spermatogonia/spermatocyte stage transcripts in a timely manner. On the other hand, later-stage spermatocytes are abnormally expressing spermiogenesis genes. Similar to the Ago4 mutant previously characterized MSCI is disrupted. The authors also show that AGO3 has different interaction partners compared to AGO4 and focus their final assessment on a novel interaction partner of AGO3, BRG1. They show that this factor, which is involved in chromatin remodeling, is aberrantly localized to the sex body during meiotic prophase and diplonema. As BRG1 is involved in open chromatin, it is proposed that AGO3 restricts BRG1 (and related proteins) from the XY chromosome to ensure MSCI. Overall, this paper is very well constructed with mechanistic insights that make this a very impactful contribution to the research community. Major Comments:

1. The abstract contains "Ago413-/- mouse" without any explanation of what that is. The abstract needs to be a stand-alone document that does not require any referencing for context.

Response: We have included a sentence describing Ago413 in line 27

Figure 2C. - The significance bars are confusing as they appear to overlap strangely.

Response: We have modified this figure and now present the significance bars are on top of the data points.

On line 235, the authors state that "we first identified the top non-overlapping upregulated genes for Ago413+/+ germ cells in each cluster. Why did the authors not also select down-regulated genes in each cluster to perform a similar analysis?

__Response: __Thank you for this question. As our goal was to identify genes that are markers of the transcriptional program in each cell type, we used only uniquely upregulated genes for each cluster. Genes that are downregulated for a cluster may be indicative of the transcription in several other cell types, which is not easily interpretable. For a revised manuscript, we will perform this analysis to determine if there is any specific alterations in these downregulated genes.

Their Ago413 mutant characterization does a good job of assessing meiotic prophase and spermatozoa. However, their assessment of the stages in between these is lacking (meiotic divisions and spermiogenesis).

Response: We understand the reviewer's concern, however, it is not usual to study stages between the first meiotic division and spermiogenesis because meiosis II is so rapid and thus we lack tools to dissect it. In general, any defect that impacts meiosis I (and particularly prophase I) leads to cell death during prophase I or at metaphase I due to strictly adhered checkpoints that eradicate defective cells. Thus, the increased TUNEL staining in prophase I indicates to us that defective cells are cleared before exit from meiosis I, and those cells progressing to the spermatid stage are "normal" for meiosis II progression. For these cells that did complete meiosis I and progressed normally through meiosis II, we analyzed their spermiogenic outcome extensively (see section entitled "Post-meiotic spermatids from Ago413-/- males exhibit defective spermiogenesis and poor spermatozoa function"). This section included extensive sperm morphology, sperm motility and sperm fertility through in vitro fertilization assays. That said, we have added a sentence on line 268 to explain the transit through meiosis II.

The discovery of the interaction between BRG1 and AGO3 is exciting. They should assess BRG1 localization in later sub-stages, including late diplonema and diakinesis.

__Response: __BRG1(SMARCA4) was analyzed throughout prophase I, as shown in image 5G, including quantification of fluorescence intensity included the analysis of diplonema (5H-I). However, diakinesis was not included here since there was no observable signal of BRG1 in these cells. We have explained this in lines 459.

ATF2 should have been assessed in more detail, as was done for BRG1 in Figure 5.

__Response: __We agree with the Reviewer, however, staining of chromosome spreads with the anti ATF2 antibody was not possible in our hands after several attempts and changes in staining conditions. However, as staining of sections was successful, we showed localization of ATF2 on spermatocytes by co staining sections with SYCP3 and ATF2.

Reviewer #3 (Significance (Required)): Overall, this paper is very well constructed with mechanistic insights, as described in my reviewer comments, that make this a very impactful contribution to the research community.

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Referee #3

Evidence, reproducibility and clarity

The authors characterize a CRISPR-Cas9 mouse mutant that targets 3 genes that encode AGO family proteins, 2 of which are expressed during spermatogenesis (AGO3 and AGO4) and one that is said is not expressed, AGO1. This mouse mutant showed that AGO3 and AGO4 both contribute to spermatogenesis success as the "Ago413" mutation gave rise to an additive reduction in testis weight, due to spermatocyte apoptosis, and reduction in sperm count. Furthermore, they use insertion mouse mutants for Ago3 and Ago2 that express tagged versions of their corresponding proteins, which they use in combination with pan-AGO antibodies and Ago mutants to show differential expression and localization properties of AGO2, AGO3, and AGO4 (and the absence of AGO1) during spermatogenesis with a particular focus on meiotic prophase. They perform single-cell RNAseq and intricate analyses to demonstrate a change in distribution of meiotic stages in Ago413 mutants, and the overall cell cycle in spermatogonia and spermatocytes is altered. This analysis shows that the mutation leads to an inability to downregulate prior spermatogonia/spermatocyte stage transcripts in a timely manner. On the other hand, later-stage spermatocytes are abnormally expressing spermiogenesis genes. Similar to the Ago4 mutant previously characterized MSCI is disrupted. The authors also show that AGO3 has different interaction partners compared to AGO4 and focus their final assessment on a novel interaction partner of AGO3, BRG1. They show that this factor, which is involved in chromatin remodeling, is aberrantly localized to the sex body during meiotic prophase and diplonema. As BRG1 is involved in open chromatin, it is proposed that AGO3 restricts BRG1 (and related proteins) from the XY chromosome to ensure MSCI. Overall, this paper is very well constructed with mechanistic insights that make this a very impactful contribution to the research community.

Major Comments:

1. The abstract contains "Ago413-/- mouse" without any explanation of what that is. The abstract needs to be a stand-alone document that does not require any referencing for context.
2. Figure 2C. - The significance bars are confusing as they appear to overlap strangely.
3. On line 235, the authors state that "we first identified the top non-overlapping upregulated genes for Ago413+/+ germ cells in each cluster. Why did the authors not also select down-regulated genes in each cluster to perform a similar analysis?
4. Their Ago413 mutant characterization does a good job of assessing meiotic prophase and spermatozoa. However, their assessment of the stages in between these is lacking (meiotic divisions and spermiogenesis).
5. The discovery of the interaction between BRG1 and AGO3 is exciting. They should assess BRG1 localization in later sub-stages, including late diplonema and diakinesis.
6. ATF2 should have been assessed in more detail, as was done for BRG1 in Figure 5.

Significance

Overall, this paper is very well constructed with mechanistic insights, as described in my reviewer comments, that make this a very impactful contribution to the research community.

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

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Referee #2

Evidence, reproducibility and clarity

In the manuscript titled "Argonaute proteins regulate the timing of the spermatogenic transcriptional program" by Carro et al., the authors present their findings on how Argonaute proteins regulate spermatogenic development. They utilize a mouse model featuring a deletion of the gene cluster on chromosome 4 that contains Ago1, Ago3, and Ago4 to investigate the cumulative roles of AGO3 and AGO4 in spermatogenic cells. The authors characterize the distribution of AGO proteins and their effects on key meiotic milestones such as synapsis, recombination, meiotic transcriptional regulation, and meiotic sex chromosome inactivation (MSCI). They analyze stage-specific transcriptomes in spermatogenic cells using single-cell and bulk RNA sequencing and determine the interactome of AGO3 and AGO4 through mass spectrometry to examine how AGO proteins may regulate gene expression in these cells during meiotic and post-meiotic development. The authors conclude that both AGO3 and AGO4 are essential for regulating the overall gene expression program in spermatogenic cells and specifically modulate MSCI to repress sex-linked genes in pachytene spermatocytes, which may be partially mediated by the proper distribution of DNA damage repair factors. Additionally, AGO3 is suggested to interact with the chromatin remodeler SWI/SNF factor BRG1, facilitating its removal from the sex-chromatin to enable the repression of sex-linked genes during MSCI.

Major Comments:

The study utilized a triple knockout mouse model to determine the effect of AGO3 on spermatogenesis, following up on their previous report about the role of AGO4 in spermatogenesis, which resulted from an upregulation of AGO3 in Ago4-/- spermatocytes. However, the results are more difficult to interpret and ascertain the role of AGO3 in these cells, given the absence of any observable phenotype from Ago3 interruption. AGO4 regulates sex body formation, meiotic sex chromosome inactivation (MSCI), and miRNA production in spermatocytes, all of which were noted in the absence of both AGO3 and AGO4, with only an increased incidence of cells containing abnormal RNAPII at the sex chromosomes. It will be necessary to characterize how AGO3 regulates spermatogenic development, including meiotic progression and the regulation of the meiotic transcriptome, and compare these findings with the current observations to determine if the proposed mechanism involving AGO3, BRG1, and possibly AP2 is relevant in this context.

Does Ago413-/- mice recapitulate the early meiotic entry phenotype observed in Ago4-/- mice? If not, could it be possible that AGO3 promotes meiotic entry, given its strong mRNA expression in spermatogonia according to the scRNAseq data (Fig. 2B) The authors suggested that the removal of BRG1 by AGO3 is necessary during sex body formation and the eventual establishment of MSCI. However, the BAF complex subunit ARID1A has been shown to facilitate MSCI by regulating promoter accessibility. It will be interesting to determine how BRG1 distribution changes across the genome in the absence of AGO proteins and how that correlates with alterations in sex-linked gene expression. The observations presented in this manuscript (Fig. 1D, 2C, 3D, and 4) suggest a haploinsufficiency of the deleted locus in spermatogenic development. How does this compare with the ablation of either Ago3 or Ago4? Please explain.

Minor Comments:

Based on the interactome analysis, it was argued that AGO3 and AGO4 may function separately. Please discuss how AGO3 might compensate for AGO4 (Line 109).<br /> In Line 221, it is unclear what is meant by 'cell cycle transcripts'. Does this refer to meiotic transcripts? It is also important to discuss the relevance of the G2/M cell cycle marker genes at later stages of meiotic prophase.<br /> While identified as a common interactor of both AGO3 and AGO4 in lines 440-445, HNRNPD is not listed among AGO4 interactors in Table S6. Please correct or explain this discrepancy. It is unclear whether wild-type cell lysate or lysate containing FLAG-tagged AGO3 was used for BRG1 immunoprecipitation, and which antibody was used to detect AGO3 in the BRG1 IP sample. A co-IP experiment demonstrating interaction between BRG1 and wild-type AGO3 would be ideal in this context. Furthermore, co-localization by IF would be beneficial to determine the subcellular localization and the cell stages the interaction may be occurring. Additionally, co-IP and Western blot methodologies should be included in the methods section. In line 599, it is unclear what is meant by 'persistence of sex chromosome de-repression'. Please correct or clarify this. If possible, please add an illustration to summarize the findings together.

Significance

Overall, this study enhances the understanding of gene expression regulation by AGO proteins during spermatogenesis. Several approaches, including functional, histological, and molecular characterization of the triple knockout phenotype, were instrumental in elucidating the role of AGO proteins in MSCI and meiotic as well as postmeiotic gene regulation. The main limitation of the study is that it is challenging to appreciate the role of AGO3 in addition to the previously published role of AGO4 without the inclusion of necessary control groups. Furthermore, the mechanism of action for AGO proteins in meiotic gene regulation was left relatively unexplored. This study presents new findings that will be significant for the research community interested in gene regulation, chromatin biology, and reproductive biology with the above suggestions considered.

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

Learn more at Review Commons

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Referee #1

Evidence, reproducibility and clarity

In their manuscript de las Mercedes Carro et al investigated the role of Ago proteins during spermatogenesis by producing a triple knockout of Ago 1, 3 and 4. They first describe the pattern of expression of each protein and of Ago2 during the differentiation of male germ cells, then they describe the spermatogenesis phenotype of triple knockout males, study gene deregulation by scRNA seq and identify novel interacting proteins by co-IP mass spectrometry, in particular BRG1/SMARCA4, a chromatin remodeling factor and ATF2 a transcription factor. The main message is that Ago3 and 4 are involved in the regulation of XY gene silencing during meiosis, and also in the control of autosomal gene expression during meiosis. Overall the manuscript is well written, the topic, very interesting and the experiments, well-executed. However, there are some parts of the methodology and data interpretation that are unclear (see below).

Major comments

1. Please clarify how the triple KO was obtained, and if it is constitutive or specific to the male germline. In the result section a Cre (which cre?) is mentioned but it is not mentioned in the M&M. On Figure S1, a MICER VECTOR is shown instead of a deletion, but nothing is explained in the text nor legend. Could the authors provide more details in the results section as well as in the M&M ? This is essential to fully interpret the results obtained for this KO line, and to compare its phenotype to other lines (such as lines 184-9 Comparison of triple KO phenotype with that of Ago4 KO). Also, if it is a constitutive KO, the authors should mention if they observed other phenotypes in triple KO mice since AGO proteins are not only expressed in the male germline.
2. The paragraph corresponding to G2/M analysis is unclear to me. Why was this analysis performed? What does the heatmap show in Figure S4? What is G2/M score? (Fig 2D). Lines 219-220, do the authors mean that Pachytene cells are in a cell phase equivalent to G2/M? All this paragraph and associated figures require more explanation to clarify the method and interpretation.
3. I have concerns regarding Fig2G: to be convincing the analysis needs to be performed on several replicates, and, it is essential to compare tubules of the same stage - which does not seem to be the case. This does not appear to be the case. Besides, co (immunofluorescent) staining with markers of different cell types should be shown to demonstrate the earlier expression of some markers and their colocalization with markers of the earlier stages.
4. one important question that I think the authors should discuss regarding their scRNAseq: clusters are defined using well characterized markers. But Ago triple KO appears to alter the timing of expression of genes... could this deregulation affects the interperetation of scRNAseq clusters and results?
5. XY gene deregulation is mentioned throughout the result section but only X chromosome genes seem to have been investigated.... Even the gene content of the Y is highly repetitive, it would be very interesting to show the level of expression of Y single copy and Y multicopy genes in a figure 3 panel.
6. Can the authors elaborate on the observation that X gene upregulation is visible in the KO before MSCI; that is in lept/zygotene clusters (and in spermatogonia, if the difference visible in 3A is significant?)
7. miRNA analysis: could the authors indicate if X encoded miRNA were identified and found deregulated? Because Ago4 has been shown to lead to a downregulation of miRNA, among which many X encoded. It is therefore puzzling to see that the triple KO does not recapitulate this observation. Were the analyses performed differently in the present study and in Ago4 KO study?
8. The last results paragraph would also benefit from some additional information. It is not clear why the authors focused on enhancers and did not investigate promoters (or maybe they were but it's unclear). Which regions (size and location from TSS) were investigated for motif enrichment analyses? To what correspond the "transcriptional regulatory regions previously identified using dREG" mentioned in the M&M? I understand it's based on a previous article, but more info in the present manuscript would be useful.

Minor comments

1. In the introduction: The sentence "Ago1 is not expressed in the germline from the spermatogonia stage onwards allowing us to use this model to study the roles of Ago4 and Ago3 in spermatogenesis." is misleading because Ago1 is expressed at least in spermatogonia; It would be more precise to write "after spermatogonia stage" and rephrase the sentence. Otherwise it is surprising to see AGO1 protein in testis lysate and it is not in line with the scRNA seq shown in figure 2.
2. Could the authors precise if AGO proteins are expressed in other tissues? In somatic testicular cells?
3. Pattern of expression: How do the authors explain that AGO3 disappears at the diplotene stage and reappears in spermatids?
4. It would be useful to show the timing of expression of AGO 1 to 4 throughout spermatogenesis in the first paragraph of the article. Maybe the authors could present data from fig2B earlier?
5. Line 190: please modify the sentence "reveal no differences in cellular architecture of the seminiferous tubules when compared to wild-type males" to " reveal no gross differences..." since even without quantification of the different cell types it is visible that KO seminiferous tubules are different from WT tubules.
6. TUNEL analysis: please stage the tubules to determine the stage(s) at which apoptosis is the most predominant.
7. Figure S4B does not show an increase of cells at Pachytene stage but at Lepto/zygotene stage (as well as an increase of spermatogonia). Please comment this discrepancy with results shown in Fig2.
8. Fig5H and 5I are not mentioned in the result section. Also, it would be useful to label them with "all chromosomes" and "XY" to differentiate them easily
9. Line 530 "data provide further evidence for a functional association between AGO-dependent small RNAs and heterochromatin formation, maintenance and/or silencing." Please rephrase, the present article does not really show that AGO nuclear role depends on small RNAs.
10. Line 1256: replace "cite here " by appropriate reference
11. Please use SMARCA4 instead of BRG1 name as it is its official name.

Figures:

Figure 1: Are the pictures shown for Ago3-tagged and floxed from the same stages ? The leptotene stage in 1A looks like a zygotene, while some pachytene/diplotene stage pictures do not look alike.

Figure 1D, please label the Y scale properly (testis weight related to body weight)

FigS1: Please comment the presence of non-specific bands in the figure legend

Fig 2E and F, please indicate on the figure (in addition to its legend), what are the X and Y axes respectively to facilitate its reading.

2F: please use an easier abbreviation for Spermatocyte than Sp (which could spermatogonia, sperm etc..) such as Scyte I ? (same comment for Fig 3C)

Overall, for all figures showing GSEA analyses, could the authors explain what a High positive NES and a High negative NES mean in the results section?

Significance

Ago proteins are known for their roles in post transcriptional gene regulation via small RNA mediated cleavage of mRNA, which takes places in the cytoplasm. Some Ago proteins have been shown to be also located in the nucleus suggesting other non-canonical roles. It is the case of Ago4 which has been shown to localize to the transcriptionally silenced sex chromosomes (called sex body) of the spermatocyte nucleus, where it contributes to regulate their silencing (Modzelewski et al 2012). Interestingly, Ago4 knockout leads to Ago3 upregulation, including on the sex body indicating that Ago3 and Ago4 are involved in the same nuclear process. In their manuscript, de las Mercedes Carro et al., investigate the consequences of loss of both Ago3 and Ago4 in the male germline by the production of a triple knockout of Ago1, 3 and 4 in the mouse. With this model, the authors describe the role of Ago3 and Ago4 during spermatogenesis and show that they are involved in sex chromosome gene repression in spermatocytes and in round spermatids, as well as in the control of autosomal meiotic gene expression. Triple KO males have impaired meiosis and spermiogenesis, with fewer and abnormal spermatozoa resulting in reduced fertility. Since Ago1 male germline expression is restricted to pre-meiotic germ cells, it is not expected to contribute to the meiotic and postmeiotic phenotypes observed in the triple KO. The strengths of the study are i) the thorough analyses of mRNA expression at the single cell level, and in purified spermatocytes and spermatids (bulk RNAseq), ii) the identification of novel nuclear partners of AGO3/4 relevant for their described nuclear role: ATF2, which they show to also co-localize with the sex body, and BRG1/SMARCA4, a SWI/SNF chromatin remodeler. The main limitation of the study is the lack of information in the method regarding the production of the triple KO, as well as some aspects of the transcriptome and motif analyses. It is also surprising to see that the triple KO does not recapitulate the miRNA deregulation observed in Ago4 KO. The characterization of a non-canonical role of AGO3/4 in male germ cells will certainly influence researchers of the field, and also interest a broader audience studying Argonaute proteins and gene regulation at transcriptional and posttranscriptional levels.

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Reply to the reviewers

Reply to the reviewers

We would like to thank the reviewers for their comments, we see great value in the suggestions they made to strengthen our work. We are glad to see that they are in general positive about the manuscript. In the following, we include a point-by-point response to their comments, which are in general consistent with each other.

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

In this manuscript, Sanchez-Cisneros and colleagues, examine how tracheal cell adhesion to the ECM underneath the epidermis helps shape the tracheal system. They show that if cell-ECM adhesion is perturbed the development of the tracheal system and the epidermis is disrupted. They also detect protrusions extending from the dorsal trunk cells towards the ECM. The work is novel, the figures are clear, and the questions are well addressed. However, I find that some of the claims are not completely supported by the data presented. I have some suggestions that will, I believe, clarify certain points.

Major comments

At the beginning of the results section as in the introduction the authors claim that "It is generally assumed that trunk displacement occurs due to tip cells pulling on the trunks so that they follow their path dorsally." This sentence is not referenced, and I do not know where it has been shown or proposed to be like this. In addition, the comparison with the ventral branches is also not referenced and the movie does not really show this. Forces generated by tracheal branch migration have been shown to drive intercalation (Caussinus E, Colombelli J, Affolter M. Tip-cell migration controls stalk-cell intercalation during Drosophila tracheal tube elongation. Curr Biol. 2008;18(22):1727-1734. doi:10.1016/j.cub.2008.10.062), but not dorsal trunk (DT) displacement.

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We agree that dorsal trunk displacement has not been discussed in previous works, just the fact that tip-cell migration influences stalk cell intercalation. We will rephrase this sentence, stating that dorsal trunk displacement has not been studied.

However, to rule out the possibility that DT displacement and the phenotype observed in XXX is due to dorsal branch pulling forces, the authors should analyze what happens in the absence of dorsal branches (in condition of Dpp signalling inhibition as in punt mutants or Dad overexpression conditions).

This is a great idea, and we thank the reviewer for suggesting this. We tried to achieve a similar goal by expressing a Dominant Negative FGFR (Breathless-DN) in the tracheal system, since its expression under btl-gal4 affects tip cell migration. However, the phenotype arises too late to have an effect in dorsal branch migration during the stages we were interested in analyzing. The alternative proposed by the reviewer should be more efficient, as blocking Dpp signalling prevents the formation of dorsal branches completely. We have just received flies carrying the UAS-Dad construct. We will express Dad under btl-gal4 and see how this affects dorsal trunk displacement.

I am concerned about the TEM observations. The authors claim they can identify tracheal cells by their lumen (Fig. 2 C'). However, at stage 15, the tracheal lumen should be clearly identifiable, and the interluminal DT space should be wider relative to the size of the cells. In this case, there is nothing telling us that we are not looking at a dorsal branch or lateral trunk cell. Furthermore, at embryonic stage 15, the tracheal lumen is filled with a chitin filament, which is not visible in these micrographs. Also, there is quite a lot of tissue detachment and empty spaces between cells, which might be a sign of problems in sample fixing. Better images and more accurate identification of dorsal trunk cells is necessary to support the claim that "These experiments revealed a novel anatomical contact between the epidermis and tracheal trunks".

The protocol that we use for TEM involves performing 1-μm sections that allow us to stage embryos and to identify the anatomical regions using light microscopy and then switch to ultra-thin sections for electron microscopy once we have found the right position within the sample. This approach also allows us to determine the integrity of the sample. We attach here a micrograph of the last section we analyzed before we decided to do the EM analysis. The asterisk (*) points to a region where the multicellular lumen of the trunk is visible. Due to its proximity to the posterior spiracles, we are confident this is the dorsal trunk and not the lateral trunk. We realize now, after comparing this image with an atlas of development (Campos-Ortega and Hartenstein, 2013), that the stage we chose to illustrate the interaction is a stage 14 embryo instead of the stage 15 we indicated in the manuscript. We will change the stage but given that dorsal closure has already started by stage 14, this does not affect our analysis. Still, we apologize for the mis-staging of the embryo.

In the light-microscopy image, we have overlaid the EM section to the corresponding region of interest. We agree that the lumen should be thicker compared to the length of the cells, if the section would be cutting the trunk through its largest diameter. However, the protrusions we see do not emerge from the middle part of the trunk where the lumen is found but are seen towards the dorsal side of the trunk, where the lumen will no longer be visible in a longitudinal section as the ones we present. In the embryo shown in Figure 2A-C, our interpretation is that the section was done through a very shallow section of the lumen (represented below). We interpret this from the fact that we see abundant electron-dense areas which we think are adherens junctions from multiple cells. These junctions are visible in Figure 2C but are currently not labelled. We will add arrows to increase their visibility.

Given that protruding cells lie at the base of dorsal branches, it would be expected that in some sections we would find the protrusions close to the dorsal branches. This is in fact what we show in the micrograph shown in Figure 2D, with a lower magnification overview image shown in Figure S2D. In this case, we see a cell in close proximity to the tendon cells on one side (Figure 2D), which is connected to a dorsal branch on the opposite side (shown in Figure S2D). This dorsal branch is clearly autocellular and chitin deposition is visible as expected for the developmental stage. Again, in Figure S2E we see an electron-dense patch near the lumen that corresponds to the adherens junctions that seal the lumen. We see that all this needs to be better explained in the manuscript, so we will elaborate on the descriptions, and incorporate the light microscopy micrograph to the supplemental figures. This should also aid with the anatomical descriptions requested by Reviewer #3. Nevertheless, we think these observations confirm that what we are describing are the contact points between the dorsal trunk and tendon cells.

Timelapse imaging of the protrusions in DT cells is done with frames every 4 minutes (Video S3). This is not enough to properly show cellular protrusions and the images do not really show interaction with the epidermis. Video S4 has a better time resolution but it is very short and only shows the cut moment. Video S4, shows the cut, but the reported (and quantified recoil) is not clear. Nevertheless, the results are noteworthy and should be further analysed.

We will acquire high temporal resolution time-lapse images using E-Cadherin::GFP and btl-gal4, UAS-PH::mCherry to show the behaviour of the protrusions on a short time scale.

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Provided these embryos survive, would it be possible to check if embryos after laser cutting will develop wavy DTs?

We think it would be interesting to carry out this experiment, but the laser cut experiments were done under a collaborative visit and we would not be able to repeat it in a short-term period.

What happens to the larvae under the genetic conditions presented in Fig.S3? Do they reach pupal stages? Do these animals reach adult stages?

We have seen escapers out of these crosses, but we have not quantified the lethality of the experiment. We will analyse this and include it in the manuscript.

The kayak phenotypes are very interesting and perhaps the authors could explore them more. As in inhibition of adhesion to the ECM, kay mutants display wavy dorsal trunks. Do they have defective adhesion? Fos being a transcription factor, this is a possibility. The authors should at least discuss the kay phenotypes more extensively and present a suitable hypothesis for the phenotype.

We agree that the kayak experiments might bring more consequences than just preventing dorsal closure. We will complement this approach by blocking dorsal closure by other independent means. We will use pannier-gal4 (a lateral epidermis driver), engrailed-gal4 (a driver for epidermal posterior compartment), and 332-gal4 (an amnioserosa driver) to express dominant-negative Moesin. In our experience, this also delays dorsal closure and it should result in a similar tracheal phenotype as the one we see in kayak embryos.

Minor comments

Page 2 Line 9/10 The sentence "tracheal tubes branch and migrate over neighbouring tissues of different biochemical and mechanical properties to ventilate them." should be rewritten. Tracheal cells do not migrate over other tissues to ventilate them.

We meant to say that tracheal cells migrate over other tissues at the same time as they branch and interconnect to allow gas exchange in their surroundings after tracheal morphogenesis is completed. Ventilation is used here as a synonym for gas exchange or breathing. We will rephrase this if the reviewer considers it confusing.

Page 2 Line 24/25 The sentence "It has been generally assumed that trunks reach the dorsal side of the embryo because of the pulling forces of dorsal branch migration." needs to be backed up by a reference.

As explained above, we will rephrase this sentence.

Page 7 Line 32/23 In this sentence, the references are not related to dorsal closure "Similarly, the signals that regulate epidermal dorsal closure do not participate in tracheal development, or vice versa (Letizia et al., 2023; Reichman-Fried et al., 1994)."

Our goal in this sentence was to explain that while JNK is required for proper epidermal dorsal closure, loss of JNK signaling in the trachea does not affect tracheal development (as shown by Letizia et al., 2023). At the same time, Reichman-Fried et al., 1994 described the phenotypes of loss of breathless (btl). We will remove this last reference as the work does not study the epidermis. We will rephrase the sentence as: “Similarly, the signals that regulate epidermal dorsal closure do not participate in tracheal development; namely, JNK signaling (Letizia et al., 2023).”

Page 12 Line 1 "Muscles attach to epidermal tendon cells through a dense meshwork of ECM" this sentence must be referenced.

We will add the corresponding references for this statement: (Fogerty et al., 1994; Prokop et al., 1998; Urbano et al., 2009). We will change “dense” for “specialized”.

Fig. S1- Single channel images (A'-C' and A'-C') should be presented in grayscale.

Fig. S4- Single channel images (A'-D' and A'-D') should be presented in grayscale.

We will add the grayscale, single-channel images for these figures.

Reviewer #1 (Significance (Required)):

The findings shown in this manuscript shed light on the interactions and cooperation between two organs, the tracheal system and the epidermis. These interactions are mediated by cell-ECM contacts which are important for the correct morphogenesis of both systems. The strengths of the work lie on its novelty and live analysis of these interactions. However, its weaknesses are related to some claims not completely backed by the data, some technical issues regarding imaging and some over-interpreted conclusions.

This basic research work will be of interest to a broad cell and developmental biology community as they provide a functional advance on the importance of cell-ECM interactions for the morphogenesis of a tubular organ. It is of specific interest to the specialized field of tubulogenesis and tracheal morphogenesis.

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

Summary: In this paper, the authors explore the relationships between two Drosophila tissues - the epidermis and tracheal dorsal trunk (DT) - that get dorsally displaced during mid-late embryogenesis. The show a nice temporal correlation between the movements of the epithelia during dorsal closure and DT displacement. They also show a correlation between the movement of an endogenously tagged version of collagen and the DT, suggesting that the ECM may contribute to this coordinated movement. Through high magnification TEM, they show that tracheal cells make direct contact with the subset of epithelial cells, known as tendon cells, that also serve as muscle attachment sites. In between these contact sites, tracheae are separated from the epithelia by the muscles. Furthermore, the TEMs and confocal imaging of tracheal cells expressing a membrane marker at these contact sites show that the tracheal cells are extending filopodia toward the tendon cells. The authors then explore how a variety of perturbations to the ECM produced by the tendon and DT cells affect DT and epithelial movement. They find that expressing membrane-associated matrix metalloproteases (MMP1 or MMP2) in tendon cells as well as perturbations in integrin or integrin signaling components leads to delays in dorsal displacement as well as defective lengthening of the tracheal DT tubes. They find that defects in the association between the tracheal and epidermal ECM attachments affect dorsal displacement of the epidermis, disrupting dorsal closure.

Major comments: I like the goals of this paper testing the idea that the ECM plays important roles in the coordination of tissue placement, and I think they have good evidence of that from this study. However, I disagree with the conclusions of the authors that disrupting contact between DT and the tendon cells has no effect on DT dorsal displacement. DT tracheal positioning is clearly delayed; the fact that it takes a lot longer indicates that the ECM does affect the process. It's just that there are likely backup systems in place - clearly not as good since the tracheal tubes end up being the wrong length.

We agree with this view; in our deGradFP experiments we see a delayed DT displacement. We focused our analyses on the coordination with epidermal remodelling, which remained unaltered, but we in fact see a delayed progression in dorsal displacement of both tissues (Figure 5I-J). We will emphasize this in the corresponding section of the Results.

It also seems important that the parts of the DT where the dorsal branches (DB) emanate are moving dorsally ahead of the intervening portions of the trachea. This suggests to me that the DB normally does contribute to DT dorsal displacement and that this activity may be what helps the DT eventually get into its final position. The authors should test whether the portions of the DT that contact the DB are under tension. If the DB migration is providing some dorsal pulling force on the DT, this may also contribute to the observed increases in DT length observed with the perturbations of the ECM between the tendon cells and the trachea - if tube lengthening is a consequence of the pulling forces that would be created by parts of the trachea moving dorsally ahead of the other parts. Here again, it would be good to test if the DT itself is under additional tension when the ECM is disrupted.

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We thank the reviewer for the suggested experiments. We agree with the fact that the dorsal branches should pull on the dorsal trunk and that this interaction should generate tension. Unfortunately, we are unable to test this with the experiments proposed by the reviewer, but we propose an alternative strategy to overcome this. We understand that the reviewer suggests we do laser cut experiments in dorsal branches to see if there is a recoil in the opposite direction of dorsal branch migration. We carried out our laser cut experiments using a 2-photon laser through a visit to the EMBL imaging facility, using funds from a collaborative grant. Funding a second visit would require us to apply for extra funding, which would delay the preparation of the experiments. We are aware of UV-laser setups within our university, however, UV-laser cuts would also affect the epidermis above the dorsal branches, which we think might contribute to recoil we would expect to see.

Instead of doing laser cuts, we have designed an experiment based on the suggestion of reviewer #1 of blocking Dpp signaling (with UAS-Dad), which would prevent the formation of dorsal branches. We expect that in this experimental setup, the trunk will bend ventrally in response to thepulling forces of the ventral branches. We will also co-express UAS-Dad (to prevent dorsal branch formation) and UAS-Mmp2 (to ‘detach’ the dorsal trunk from the epidermis), and we would expect to at least partially rescue the wavy trunk phenotype.

Minor comments: The authors need to do a much better job in the intro and in the discussion of citing the work of the people who made many of the original findings that are relevant to this study. Many citations are missing (especially in the introduction) or the authors cite their own review (which most people will not have read) for almost everything (especially in the discussion). This fails to give credit to decades of work by many other groups and makes it necessary for someone who would want to see the original work to first consult the review before they can find the appropriate reference. I know it saves space (and effort) but I think citing the original work is important.

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The reviewer is right; we apologize for falling into this practice. We will reference the original works wherever it is needed.

Figure 7 is not a model. It is a cartoon depicting what they see with confocal and TEM images.

We will change the figure; we will include our interpretations of the phenotypes we observed under different experimental manipulations.

Reviewer #2 (Significance (Required)):

Overall, this study is one of the first to focus on how the ECM affects coordination of tissue placement. The coordination of tracheal movement with that of the epidermis is very nicely documented here and the observation that the trachea make direct contact with the tendon cells/muscle attachment sites is quite convincing. It is less clear from the data how exactly the cells of the trachea and the ECM are affected by the different perturbations of the ECM. It seems like this could be better done with immunostaining of ECM proteins (collagen-GFP?), cell type markers, and super resolution confocal imaging with combinations of these markers. What happens right at the contact site between the tendon cell and the trachea with the perturbation? I think that at the level of analysis presented here, this study would be most appropriate for a specialized audience working in the ECM or fly embryo development field.

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

Summary The manuscript by Sanchez-Cisneros et al provides a detailed description of the cellular interactions between cells of the Drosophila embryonic trachea and nearby tendon and epidermal cells. The researchers use a combination of genetic experiments, light sheet style live imaging and transmission electron microscopy. The live imaging is particularly clear and detailed, and reveals protruding cells. The results overall suggest that interactions mediated through the ECM contribute to development of trachea and dorsal closure of epidermis. One new aspect is the existence of dorsal trunk filipodia that are under tension and may impact tracheal morphogenesis through required integrin/ECM interactions.

Major comments: - Are the key conclusions convincing? Generally, the key conclusions are well supported by the data, and the movies are very impressive. Interactions between the cell types are clearly shown, as is the correlations in their development. However, some of the images are challenging to decipher for a non-expert in Drosophila trachea, especially the EM images, and some of the data is indirect or a bit weak.

We thank the reviewer for their observations. As mentioned above in response to Reviewer #1, we will add an overview image of the embryo we processed for TEM that is presented in Figure 2.

The data related to failure of dorsal closure affecting trachea relies on one homozygous allele of one gene (kayak), and so this is somewhat weak evidence. Even though kay is not detected in trachea, there could be secondary effects of the mutation or another lesion on the mutant chromosome. The segments look a bit uneven in the mutant examples.

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The reviewer is right; as we proposed before, we will complement the kayak experiments with independent approaches that will delay dorsal closure.

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? Some of the experiments have low n values, especially in imaging experiments, so these may be more preliminary, but they are in concordance with other data.

The problem we face in our live-imaging experiments is related to the probability of finding the experimental embryos. In most of our experiments we combine double-tissue labelling plus the expression of genetic tools. This generally corresponds to a very small proportion of the progeny. We will aim to have at least 4 embryos per condition.

• 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. Higher n-values would substantiate the claims. To strengthen the argument that dorsal closure affects trachea morphogenesis mechanically, the authors might consider using of a combination of kay mutant alleles or other mutant genes in this pathway to provide stronger evidence. Or they could try a rescue experiment in epidermis and trachea separately for the kay mutants.

We think our experiments delaying dorsal closure using the Gal4/UAS system and a variety of drivers should address the point of the possible indirect effects of kay in tracheal development.

• 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. Imaging data can take awhile to obtain, but the genetic experiments could be done in a couple of months, and the authors should be able to obtain any needed lines within a few weeks.

The reviewer is correct, we will be able to plan our crosses for the proposed experiments within a couple of months.

• Are the data and the methods presented in such a way that they can be reproduced? Generally, yes. For the deGrad experiments, it is not clear how the fluorescent intensity was normalized - was this against a reference marker?

Briefly, we used signals from within the embryo as internal controls. In the case of en-gal4, we normalized the signal to the sections of the embryo where en is not expressed and therefore, beta-integrin levels should not be affected. In the case of btl-gal4, we normalized against the signal surrounding the trunks which should also not be affected by the deGradFP system. We will elaborate on these analyses in the methods section.

Are the experiments adequately replicated and statistical analysis adequate? There are several experiments with low n values, so this could fall below statistical significance. For example, data shown in Fig 1G: n=3; Fig 4D n=4, n=3; Fig 6J n=4

As mentioned above, we will increase our sample sizes.

Minor comments: - Specific experimental issues that are easily addressable. To make the TEM images more easily interpreted, it would be helpful to provide a fluorescent image of all the relevant cell types (especially trachea, epidermis, muscle, and tendon cells, plus segmental boundaries) labelled accordingly, so that reader can correlate them more easily with the TEM images. They might also include a schematic of an embryo to show where the TEM field of view is.

We believe this should be addressed by adding the light microscopy section of the embryo with the TEM image overlaid as illustrated above.

It is hard to be confident that the EM images reflect the cells they claim and that the filopodia are in fact that, at least for people not used to looking at these types of images.

As we explained in the response to Reviewer #1, we will elaborate on the descriptions of our TEM data. We think that adding the reference micrograph will aid with the interpretations of the TEM images.

• Are prior studies referenced appropriately? yes

• Are the text and figures clear and accurate? yes

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? The writing could be revised to be a bit clearer. Since the results of the experiments do not support the initial hypothesis, I found it a bit confusing as I read along. It may help to introduce an alterative hypothesis earlier to make the paper more logical and easy to follow. To be more specific, On page 3, the authors say they "show that dorsal trunk displacement is mechanically coupled to the remodelling of the epidermis" and also in the results comment that "With two opposing forces pulling the trunks other factors likely participate in their dorsal displacement, but so far these have remained unstudied." But that doesn't end up being what they find. The results from figure 5 and related interpretation on page 17 says "cell-ECM interactions are important for proper trunk morphology, but not for its displacement." So this was confusing to read and I would encourage the authors to frame the issues a bit differently in terms of tube morphogenesis.

We see how this might be confusing. We will rewrite the introduction so that the work is easier to follow. To achieve this, we will state from the beginning the mechanisms we anticipate that regulate trunk displacement: 1) adhesion to the epidermis, 2) pulling forces from the dorsal branches and 3) a combination of both.

Some minor presentation issues: What orientation is the cross-sectional view in figure 1C and movie 1?

We will add a dotted box that indicates the region that we turned 90° to show the cross-section.

On page 12, the authors say the "Electron micrographs also suggested high filopodial activity" but activity suggests dynamics that are not clear from EM. This could be re-phrased.

As the reviewer indicates, we cannot conclude dynamics from a static image. We will replace “suggested high filopodial activity” with “revealed filopodial abundance”.

Reviewer #3 (Significance (Required)):

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field. The results of the paper are significant in that they characterize a mechanical interaction between two tissue types in development, which are linked by the extracellular matrix that sits between them. It is not clear to me that this describes a "novel mechanism for tissue coordination" as stated in the abstract, but it does characterize this type of interaction in a detailed cellular way.

• Place the work in the context of the existing literature (provide references, where appropriate). For specialists, the work identifies a novel protruding cell type in the fly embryonic trachea, and provides beautiful and detailed imaging data on tracheal development. The "wavy" trachea phenotype is also uncommon and very interesting, so this result could be linked to the few papers that also describe this phenotype and be built up.

• State what audience might be interested in and influenced by the reported findings. As it stands, this is most interesting for a specialized audience because it requires some understanding of the development of this system in particular. As it characterizes this to a new level of detail, it could be influential to those in the field. Some addition clarification of the results and re-framing could make the manuscript more clear and interesting for non-specialists.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. I work with Drosophila and have studied embryonic and adult cell types, although not trachea specifically. I am familiar with all the genetic techniques and imaging techniques used here.

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Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript by Sanchez-Cisneros et al provides a detailed description of the cellular interactions between cells of the Drosophila embryonic trachea and nearby tendon and epidermal cells. The researchers use a combination of genetic experiments, light sheet style live imaging and transmission electron microscopy. The live imaging is particularly clear and detailed, and reveals protruding cells. The results overall suggest that interactions mediated through the ECM contribute to development of trachea and dorsal closure of epidermis. One new aspect is the existence of dorsal trunk filipodia that are under tension and may impact tracheal morphogenesis through required integrin/ECM interactions.

Major comments:

• Are the key conclusions convincing?

Generally, the key conclusions are well supported by the data, and the movies are very impressive. Interactions between the cell types are clearly shown, as is the correlations in their development. However, some of the images are challenging to decipher for a non-expert in Drosophila trachea, especially the EM images, and some of the data is indirect or a bit weak.

The data related to failure of dorsal closure affecting trachea relies on one homozygous allele of one gene (kayak), and so this is somewhat weak evidence. Even though kay is not detected in trachea, there could be secondary effects of the mutation or another lesion on the mutant chromosome. The segments look a bit uneven in the mutant examples. - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

Some of the experiments have low n values, especially in imaging experiments, so these may be more preliminary, but they are in concordance with other data. - 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.

Higher n-values would substantiate the claims. To strengthen the argument that dorsal closure affects trachea morphogenesis mechanically, the authors might consider using of a combination of kay mutant alleles or other mutant genes in this pathway to provide stronger evidence. Or they could try a rescue experiment in epidermis and trachea separately for the kay mutants. - 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.

Imaging data can take awhile to obtain, but the genetic experiments could be done in a couple of months, and the authors should be able to obtain any needed lines within a few weeks. - Are the data and the methods presented in such a way that they can be reproduced?

Generally, yes. For the deGrad experiments, it is not clear how the fluorescent intensity was normalized - was this against a reference marker? - Are the experiments adequately replicated and statistical analysis adequate?

There are several experiments with low n values, so this could fall below statistical significance. For example, data shown in Fig 1G: n=3; Fig 4D n=4, n=3; Fig 6J n=4

Minor comments:

• Specific experimental issues that are easily addressable.

To make the TEM images more easily interpreted, it would be helpful to provide a fluorescent image of all the relevant cell types (especially trachea, epidermis, muscle, and tendon cells, plus segmental boundaries) labelled accordingly, so that reader can correlate them more easily with the TEM images. They might also include a schematic of an embryo to show where the TEM field of view is.

It is hard to be confident that the EM images reflect the cells they claim and that the filopodia are in fact that, at least for people not used to looking at these types of images. - Are prior studies referenced appropriately?

yes - Are the text and figures clear and accurate?

yes - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

The writing could be revised to be a bit clearer. Since the results of the experiments do not support the initial hypothesis, I found it a bit confusing as I read along. It may help to introduce an alterative hypothesis earlier to make the paper more logical and easy to follow. To be more specific, On page 3, the authors say they "show that dorsal trunk displacement is mechanically coupled to the remodelling of the epidermis" and also in the results comment that "With two opposing forces pulling the trunks other factors likely participate in their dorsal displacement, but so far these have remained unstudied." But that doesn't end up being what they find. The results from figure 5 and related interpretation on page 17 says "cell-ECM interactions are important for proper trunk morphology, but not for its displacement." So this was confusing to read and I would encourage the authors to frame the issues a bit differently in terms of tube morphogenesis.

Some minor presentation issues:

What orientation is the cross-sectional view in figure 1C and movie 1? On page 12, the authors say the "Electron micrographs also suggested high filopodial activity" but activity suggests dynamics that are not clear from EM. This could be re-phrased.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

The results of the paper are significant in that they characterize a mechanical interaction between two tissue types in development, which are linked by the extracellular matrix that sits between them. It is not clear to me that this describes a "novel mechanism for tissue coordination" as stated in the abstract, but it does characterize this type of interaction in a detailed cellular way. - Place the work in the context of the existing literature (provide references, where appropriate).

For specialists, the work identifies a novel protruding cell type in the fly embryonic trachea, and provides beautiful and detailed imaging data on tracheal development. The "wavy" trachea phenotype is also uncommon and very interesting, so this result could be linked to the few papers that also describe this phenotype and be built up. - State what audience might be interested in and influenced by the reported findings.

As it stands, this is most interesting for a specialized audience because it requires some understanding of the development of this system in particular. As it characterizes this to a new level of detail, it could be influential to those in the field. Some addition clarification of the results and re-framing could make the manuscript more clear and interesting for non-specialists. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I work with Drosophila and have studied embryonic and adult cell types, although not trachea specifically. I am familiar with all the genetic techniques and imaging techniques used here.

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Referee #2

Evidence, reproducibility and clarity

Summary: In this paper, the authors explore the relationships between two Drosophila tissues - the epidermis and tracheal dorsal trunk (DT) - that get dorsally displaced during mid-late embryogenesis. The show a nice temporal correlation between the movements of the epithelia during dorsal closure and DT displacement. They also show a correlation between the movement of an endogenously tagged version of collagen and the DT, suggesting that the ECM may contribute to this coordinated movement. Through high magnification TEM, they show that tracheal cells make direct contact with the subset of epithelial cells, known as tendon cells, that also serve as muscle attachment sites. In between these contact sites, tracheae are separated from the epithelia by the muscles. Furthermore, the TEMs and confocal imaging of tracheal cells expressing a membrane marker at these contact sites show that the tracheal cells are extending filopodia toward the tendon cells. The authors then explore how a variety of perturbations to the ECM produced by the tendon and DT cells affect DT and epithelial movement. They find that expressing membrane-associated matrix metalloproteases (MMP1 or MMP2) in tendon cells as well as perturbations in integrin or integrin signaling components leads to delays in dorsal displacement as well as defective lengthening of the tracheal DT tubes. They find that defects in the association between the tracheal and epidermal ECM attachments affect dorsal displacement of the epidermis, disrupting dorsal closure.

Major comments: I like the goals of this paper testing the idea that the ECM plays important roles in the coordination of tissue placement, and I think they have good evidence of that from this study. However, I disagree with the conclusions of the authors that disrupting contact between DT and the tendon cells has no effect on DT dorsal displacement. DT tracheal positioning is clearly delayed; the fact that it takes a lot longer indicates that the ECM does affect the process. It's just that there are likely backup systems in place - clearly not as good since the tracheal tubes end up being the wrong length. It also seems important that the parts of the DT where the dorsal branches (DB) emanate are moving dorsally ahead of the intervening portions of the trachea. This suggests to me that the DB normally does contribute to DT dorsal displacement and that this activity may be what helps the DT eventually get into its final position. The authors should test whether the portions of the DT that contact the DB are under tension. If the DB migration is providing some dorsal pulling force on the DT, this may also contribute to the observed increases in DT length observed with the perturbations of the ECM between the tendon cells and the trachea - if tube lengthening is a consequence of the pulling forces that would be created by parts of the trachea moving dorsally ahead of the other parts. Here again, it would be good to test if the DT itself is under additional tension when the ECM is disrupted.

Minor comments: The authors need to do a much better job in the intro and in the discussion of citing the work of the people who made many of the original findings that are relevant to this study. Many citations are missing (especially in the introduction) or the authors cite their own review (which most people will not have read) for almost everything (especially in the discussion). This fails to give credit to decades of work by many other groups and makes it necessary for someone who would want to see the original work to first consult the review before they can find the appropriate reference. I know it saves space (and effort) but I think citing the original work is important.

Figure 7 is not a model. It is a cartoon depicting what they see with confocal and TEM images.

Significance

Overall, this study is one of the first to focus on how the ECM affects coordination of tissue placement. The coordination of tracheal movement with that of the epidermis is very nicely documented here and the observation that the trachea make direct contact with the tendon cells/muscle attachment sites is quite convincing. It is less clear from the data how exactly the cells of the trachea and the ECM are affected by the different perturbations of the ECM. It seems like this could be better done with immunostaining of ECM proteins (collagen-GFP?), cell type markers, and super resolution confocal imaging with combinations of these markers. What happens right at the contact site between the tendon cell and the trachea with the perturbation? I think that at the level of analysis presented here, this study would be most appropriate for a specialized audience working in the ECM or fly embryo development field.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Sanchez-Cisneros and colleagues, examine how tracheal cell adhesion to the ECM underneath the epidermis helps shape the tracheal system. They show that if cell-ECM adhesion is perturbed the development of the tracheal system and the epidermis is disrupted. They also detect protrusions extending from the dorsal trunk cells towards the ECM.

The work is novel, the figures are clear, and the questions are well addressed. However, I find that some of the claims are not completely supported by the data presented. I have some suggestions that will, I believe, clarify certain points.

Major comments

At the beginning of the results section as in the introduction the authors claim that "It is generally assumed that trunk displacement occurs due to tip cells pulling on the trunks so that they follow their path dorsally." This sentence is not referenced, and I do not know where it has been shown or proposed to be like this. In addition, the comparison with the ventral branches is also not referenced and the movie does not really show this. Forces generated by tracheal branch migration have been shown to drive intercalation (Caussinus E, Colombelli J, Affolter M. Tip-cell migration controls stalk-cell intercalation during Drosophila tracheal tube elongation. Curr Biol. 2008;18(22):1727-1734. doi:10.1016/j.cub.2008.10.062), but not dorsal trunk (DT) displacement. However, to rule out the possibility that DT displacement and the phenotype observed in XXX is due to dorsal branch pulling forces, the authors should analyze what happens in the absence of dorsal branches (in condition of Dpp signalling inhibition as in punt mutants or Dad overexpression conditions).

I am concerned about the TEM observations. The authors claim they can identify tracheal cells by their lumen (Fig. 2 C'). However, at stage 15, the tracheal lumen should be clearly identifiable, and the interluminal DT space should be wider relative to the size of the cells. In this case, there is nothing telling us that we are not looking at a dorsal branch or lateral trunk cell. Furthermore, at embryonic stage 15, the tracheal lumen is filled with a chitin filament, which is not visible in these micrographs. Also, there is quite a lot of tissue detachment and empty spaces between cells, which might be a sign of problems in sample fixing. Better images and more accurate identification of dorsal trunk cells is necessary to support the claim that "These experiments revealed a novel anatomical contact between the epidermis and tracheal trunks".

Timelapse imaging of the protrusions in DT cells is done with frames every 4 minutes (Video S3). This is not enough to properly show cellular protrusions and the images do not really show interaction with the epidermis. Video S4 has a better time resolution but it is very short and only shows the cut moment. Video S4, shows the cut, but the reported (and quantified recoil) is not clear. Nevertheless, the results are noteworthy and should be further analysed. Provided these embryos survive, would it be possible to check if embryos after laser cutting will develop wavy DTs?

What happens to the larvae under the genetic conditions presented in Fig.S3? Do they reach pupal stages? Do these animals reach adult stages?

The kayak phenotypes are very interesting and perhaps the authors could explore them more. As in inhibition of adhesion to the ECM, kay mutants display wavy dorsal trunks. Do they have defective adhesion? Fos being a transcription factor, this is a possibility. The authors should at least discuss the kay phenotypes more extensively and present a suitable hypothesis for the phenotype.

Minor comments

Page 2 Line 9/10 The sentence "tracheal tubes branch and migrate over neighbouring tissues of different biochemical and mechanical properties to ventilate them." should be rewritten. Tracheal cells do not migrate over other tissues to ventilate them.

Page 2 Line 24/25 The sentence "It has been generally assumed that trunks reach the dorsal side of the embryo because of the pulling forces of dorsal branch migration." needs to be backed up by a reference.

Page 7 Line 32/23 In this sentence, the references are not related to dorsal closure "Similarly, the signals that regulate epidermal dorsal closure do not participate in tracheal development, or vice versa (Letizia et al., 2023; Reichman-Fried et al., 1994)."

Page 12 Line 1 "Muscles attach to epidermal tendon cells through a dense meshwork of ECM" this sentence must be referenced.

Fig. S1- Single channel images (A'-C' and A'-C') should be presented in grayscale.

Fig. S4- Single channel images (A'-D' and A'-D') should be presented in grayscale.

Significance

The findings shown in this manuscript shed light on the interactions and cooperation between two organs, the tracheal system and the epidermis. These interactions are mediated by cell-ECM contacts which are important for the correct morphogenesis of both systems. The strengths of the work lie on its novelty and live analysis of these interactions. However, its weaknesses are related to some claims not completely backed by the data, some technical issues regarding imaging and some over-interpreted conclusions.

This basic research work will be of interest to a broad cell and developmental biology community as they provide a functional advance on the importance of cell-ECM interactions for the morphogenesis of a tubular organ. It is of specific interest to the specialized field of tubulogenesis and tracheal morphogenesis.

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Reply to the reviewers

We thank the reviewers for their careful and thoughtful read of our work.

Reviewer 1 helpfully suggested that the audience might not know what fuzzy matching is. The manuscript contains the following explanation of fuzzy matching:

"That subjects had almost no exact matches to SARS-CoV-2-specific IGH sequences did not exclude the possibility that they have sequences that are functionally similar to these reference sequences. The same possibility exists for TRBs. A standard method for finding similar sequences is using the Levenshtein (edit) distance. Sequences with a distance of less than or equal to a tolerance t are considered similar (for example, sequences that differ by no more than t=1 amino acid). This is known as “fuzzy matching” with tolerance t. (Note that exact matches are just fuzzy matches with tolerance 0.)"

We now also add the word "approximate" in conjunction with earlier uses of the word "fuzzy."

Reviewer 2 asked whether we "focused on potential contributions [to CDR3 length variations] based on germline gene usage, rather than directly observed contributions from the V and J segments within the CDR3 regions;" the answer is, the latter. Reviewer 2 also pointed out that it would be valuable to have HLA typing for a more comprehensive analysis. We wholeheartedly agree and have added a sentence to this effect in the discussion.

Reviewer 3 had several specific comments. The first was regarding the overall implication of the study. There are several:

• binding capacity is as predictive as, and more robust than, prior approaches. As we write: "We found that repertoires’ binding capacity to known SARS-CoV-2-specific CD4+ TRBs performs as well as the best hand-tuned approximate or “fuzzy” matching at predicting a protective level of NAbs, while also being more robust to repertoire sample size and not requiring hand-tuning."

• the importance of looking for unexpected patterns, for example in non-productive joins as was done here, and for global small-scale perturbations that together result in unavoidable signals. As we write, "B- and T-cell adaptive responses to SARS-CoV-2 infection and vaccination are surprising, subtle, and diffuse," and "One open question is to what extent infection affects antibody and TCR repertoires as a whole vs. enriching specific clones within it. One can refer to these ends of the continuum of possible effects as “diffuse” vs. “precise.”"

• caution against over-interpreting correlations with specific gene segments and. As we write: "With these caveats in mind, to our knowledge previous studies have identified 20 IGH V genes to be enriched in sequences produced during various immune responses to SARS-CoV-2.8–16 Given that human genomes encode 54 IGH V genes,17 collectively these studies implicate 37% of V genes in the response to this single viral exposure, indicating that the SARS-CoV-2 response is either quite broad within individuals, quite heterogeneous among individuals, or both."

Each of these challenges prevailing approaches, understanding, and conclusions about patterns and signatures in repertoire sequence. We should hope this would be of some benefit.

Reviewer 3 also asked what type of vaccines the participants received. We have now clarified that they all received an mRNA vaccine: 80% receiving Pfizer Comirnaty and the rest receiving Moderna Spikevax.

We looked at anti-spike neutralizing antibodies because this is where the evidence for neutralization is strongest. It would have been great to have diagnostics for every protein as well as Fc function, but these were not available and therefore not possible to study.

Reviewer 3 noted that we mention that it is impossible to know a priori what study size would be adequate to identify public sequences comprehensively in COVID-19 and asks if 251 individuals are enough. Assuming this is in reference to the size of our study, we would like to point out that this study does not claim to identify public sequences comprehensively. The rationale is more is better. The statistics tell the reader the extent to which to reject the null hypotheses put forth.

Regarding comorbidities: we probably could perform an analysis on their impact in a future study. We thank the reviewer for this idea.

Regarding timing: samples were collected from the vaccinee cohort 4 to 84 days (mean = 44.3 days, standard deviation = 15.3 days) after administration of the initial vaccine dose. Supplementary Figure S13 shows sampling times vs. NAb titers.

We feel the length of the introduction is required to contextualize the implications and benefits of this study.

We were unable to find the typos referred to but did run the manuscript through spelling and grammar checks again. We thank the Reviewer for the thoughtful attentiveness.

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Referee #3

Evidence, reproducibility and clarity

This study by Braun et al. looked at B and T cell receptor repertoires in SARS-CoV-2 infected and vaccinated individuals in comparison to healthy controls to evaluate the impact on neutralizing antibody titers. The results are clearly presented. As expected, vaccination and infection have differential effects on the repertoires. The major finding is that vaccinated and infected individuals with more SARS-CoV-2-specific TRBs have higher neutralizing antibody titers.

Major comments:

• It is not clear what the overall implication of this study is? What are the benefits?

• The authors did not specify what type of vaccines the participants received. If different vaccines were used, a comparison is necessary.

• The authors only looked at anti-spike neutralizing antibodies while other SARS-CoV-2 proteins could have a different impact. It is also known that Fc-functions participate to protection and should be studied.

• Line 55 the authors mentioned it's difficult to know what study size is enough to represent the population. What is the rationale for including 251 individuals? Is this enough to represent the population?

• With so many comorbidities in the different cohorts, could the authors perform an analysis of the impact of such comorbidities?

• The timing of the SARS-CoV-2 infection or vaccination of the individuals is missing. Were all samples collected at the same time? As we know neutralizing antibodies are waning over time, it is important to include this data.

Minor comments:

• Introduction is quite long and needs to be summarized better.

• Include a table with all the abbreviations

• Missing data in the individuals demographics table

• Typo line 65

• Typo in the methods section

Significance

This study highlights the effects of SARS-CoV-2 vaccination versus infection on antibody and T cell repertoires. Increasing evidence shows the differential effects of vaccination compared to infection. This substantial study provides new data to the field. However, for a virus for which many vaccines and treatments have already been developed and proven effective, the implications and benefits to the field should be more clearly explained.

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Referee #2

Evidence, reproducibility and clarity

SUMMARY

The paper focuses on identifying signatures in specific antibody and T-cell receptor repertoires related to SARS-CoV-2 infection and vaccination within a cohort of 250 patients. This study addresses the limitations of prior research, which often relied on small sample sizes, possibly leading to an underestimation of the variability in adaptive immune responses to SARS-CoV-2 infection and vaccination. Researchers analyzed functional features by sequencing IGH, TRD, and TRB, aiming to identify signatures that correlate antibody and T-cell responses with SARS-CoV-2 exposure.

MAJOR COMMENTS

• The study's major limitations, as acknowledged by the authors, primarily relate to the timing of sample collections during the pandemic and current methodological constraints, such as the challenge of reliably predicting receptor-antigen binding using a unified approach. Despite these challenges, the methodologies and statistical approaches employed were carefully designed to minimize potential biases. The tools and findings from this study could prove valuable for future research, particularly in this rapidly evolving field.

• One intriguing finding was the observed pattern of IGH CDR3 lengths among vaccinated individuals. When investigating the contributions of germline genes to CDR3 regions as a potential explanation for length variations, did I understand correctly that authors focused on potential contributions based on germline gene usage, rather than directly observed contributions from the V and J segments within the CDR3 regions? This discovery highlights a potential impact of vaccination on V-D-J recombination machinery.

• OPTIONAL For future studies, it may be valuable to have HLA typing for a more comprehensive analysis.

Significance

Overall, this manuscript uncovers previously undescribed patterns of immune responses to SARS-CoV-2 infection and vaccination. It is supported by a statistically robust methodological approach to effectively interpret the complex features resulting from exposure to a specific immunogen.

The manuscript could be of broad interest for immunologists, clinicians and bioinformaticians.

My area of expertise lies in the molecular biology of T cells, with a focus on applying multi-omics approaches (e.g., transcriptomics, epigenomics) to elucidate the molecular mechanisms governing T cell function and their role in the immune responses.

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Referee #1

Evidence, reproducibility and clarity

In this study, the authors sequenced B- and T-cell receptor repertoires (recombined immunoglobulin heavy-chain, TCRβ, and TCRδ genes) from the blood of infected, vaccinated, and control subjects (tested for negative). They focused on their hypervariable CDR3 regions and correlated this AIRRseq data with demographics and clinical findings from subject data. They investigated whether features of these repertoires could predict subjects' SARS-CoV-2 neutralizing antibody titer. They discovered that age affected NAb levels in vaccinated subjects but not infectees. Furthermore, they found that vaccination, but not infection, substantially affects non-productively recombined IGHs, and that repertoires' binding capacity to known SARS-CoV-2-specific CD4+ TCRβ performs as well as the best matching at predicting a protective level of NAbs. The overall conclusion from this dataset is that B- and T-cell adaptive responses to SARS-CoV-2 infection and vaccination are subtle and diffuse.

The data support the claims and the conclusions and do not require additional analyses.

The study is robust and large, with over 250 subjects, and involved sequencing IGH and TCRdelta as well as TCRbeta, to a depth of over 100000 cells/subject.

Significance

The study is very specific and sectorial, and I do not think it is easily accessible to a broad audience of immunologists; despite this, however, the authors have managed to explain quite understandably the results achieved, the challenges faced, and the conclusions obtained. If the aim is to inform the scientific community that deals with immunology, I suggest not assuming that the audience knows what fuzzy is. So, I would recommend explaining the statistical tools used in a few words.

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Reply to the reviewers

1.1. It would be helpful if the authors could discuss whether there is any correlation between cryptic sites and the extent of experimental validation in the Phosphosite database (e.g. those that were only identified in one or a few MS experiments). It is difficult to determine stoichiometry of phosphorylation experimentally, but can any inference be made on the extent of phosphorylation of cryptic sites vs. more conventional sites located in IDRs or on the surface of globular domains?

We thank the reviewer for this valuable suggestion. To investigate the extent of the experimental validation of phosphosites, we examined the number of supporting studies for each site reported in the PhosphoSitePlus database. Specifically, we summed the values of the LT_LIT (literature-based experiments), MS_LIT (mass spectrometry literature), and MS_CST (Cell Signaling Technology mass spectrometry) fields to count the number of independent studies supporting each phosphorylation site, either cryptic or non-cryptic. To visualize the results, we plotted the number of supporting references vs the relative solvent accessibility (RSA) distribution of phosphosites (Figure R1). The analysis revealed a direct correlation between the RSA of phosphosites and the number of studies supporting their phosphorylation. This observation may arise from an intrinsic difficulty in studying cryptic phosphosites due to their destabilizing effects on native proteins. Notably, no differences were observed in the number of supporting studies within cryptic phosphosites (Figure R1B). We have not mentioned these analyses in the new version of the manuscript. However, we would gladly add it if the editor or the reviewer advises accordingly.

1.2. The authors note that a larger percentage of tyrosine phosphorylation sites are cryptic compared with serine/threonine sites. I assume that tyrosine itself is more highly enriched in the hydrophobic cores of proteins relative to serine or threonine, due to its bulky hydrophobic side chain. Is the increased proportion of cryptic tyrosine phosphorylation sites more, less, or the same as the proportion of tyrosine in hydrophobic cores relative to serine and threonine?

We thank the reviewer for this insightful comment. As correctly noted, tyrosine residues tend to be enriched in the hydrophobic cores of proteins, as reflected by their generally lower relative solvent accessibility (RSA) values, regardless of phosphorylation state. This enrichment is likely due to the tyrosine side chain's bulky and partially hydrophobic nature. To address the reviewer's question, we compared the RSA distributions of phosphorylated tyrosine, serine, and threonine residues with that of the same residues non-phosphorylated in the human proteome (Figure R2). In order to statistically compare the two distributions, we employed the Mann-Whitney test. The large sample size inevitably yields very low p-values, even when the distributions differ mildly (pThr, pSer vs non-p Thr, Ser, p 1.3. Fig. 5D and E: I had some trouble interpreting these figures. Indicating where the native state is in the plots would be helpful (stated in text as lower right, but a rectangle on the plot would make this more obvious). The text discusses three metastable intermediates, but what is the fourth one shown on the figures (well A, close to the native state)? This could be more explicitly explained.

We added the missing rectangles into the original Fig. 5D and E (see below Figure R3 and R4). The three metastable intermediates discussed in the original text reflect protein conformers in which the cryptic site is exposed to the solvent. Conversely, the fourth state, and the final native state, are conformations in which the site is already partially or fully cryptic. The observation that the masking of cryptic sites coincides with the latest folding steps allows us to hypothesize a mechanism by which cryptic phosphorylation may regulate protein folding. Following the reviewer's suggestion, we now specify more explicitly each conformation in the new version of the legends of the relative figures (text file with track changes, lines 950 and 1017).

1.4. The fact that phosphomimetic mutations of cyptic sites in SMAD2 and CHK1 lead to lower expression levels and shorter half-lives is not surprising, given the expected disruption of the hydrophobic core by introduction of a charged residue. The results certainly show that if phosphorylated, these sites would decrease expression and half-life. With respect to half-life, however, if the authors are correct and cryptic sites are predominately phosphorylated co-translationally, one would expect that the half-life curves for the wt protein would not be a simple exponential, but would instead reflect two distinct populations: those that are phosphorylated during translation, and are almost immediately degraded, and those that escape phosphorylation and have the same half-life as the non-phosphorylatable mutant. Are the actual experimental results consistent with this two-population model? If not, this would be evidence that some of these cryptic sites can be exposed post-translation, either by thermal fluctuation or biological interactions.

We thank the reviewer for this insightful point. The readout employed in our study (i.e., western blotting) measures the aggregate signal from the total protein population in the cell culture. It thus reflects average protein levels rather than the dynamics of individual molecules. As such, it is not well-suited to resolving coexisting populations with distinct half-lives. We agree that if phosphorylation of cryptic sites occurs strictly co-translationally, one might expect a biphasic decay curve. However, due to methodological constraints, our assay provides only a single exponential fit to the global turnover kinetics. While we cannot entirely exclude the possibility that cryptic sites may become exposed post-translationally (e.g., due to thermal fluctuations or interactions), our molecular dynamics simulations did not reveal such exposure events within the simulated timescales. Therefore, while the two-population model remains plausible in principle, our results are consistent with a co-translational phosphorylation and degradation model. Forthcoming experiments aimed at characterizing the phosphorylation of ribosome-associated nascent chains in the human proteome may further validate this conclusion.

1.5. The authors make a point that cryptic phosphosites are more highly conserved than non-cryptic phosphosites, but it is not clear to me whether it is the side chain itself or its ability to be phosphorylated that is conserved. Supplemental Fig. 9, if I am interpreting it correctly, would suggest it is the residue itself and not its phosphorylation that is conserved. If so, wouldn't this suggest that phosphorylation of these cryptic sites is just an inevitable consequence of the conservation of serine, threonine, and tyrosine residues in hydrophobic core regions? If the authors have evidence that argues against this simple hypothesis, they should discuss it (e.g., cryptic phosphosites are more highly conserved in some cases than non-phosphorylated tyrosine, serine, and threonine residues that are not solvent accessible).

We agree with the reviewer's interpretation. The higher conservation of cryptic phosphosites likely reflects the evolutionary constraint on hydrophobic core residues, which tend to be more conserved due to their role in structural stability. This conservation does not imply phosphorylation at those sites is functionally selected across species. Instead, when such residues are phosphorylated, as we observe in the human proteome, the effect is often destabilizing and associated with protein degradation. Our analysis does not establish that the phosphorylation of cryptic residues is conserved across species, only that the residues themselves are. We appreciate the reviewer's suggestion and now explicitly discuss this point in the revised manuscript to clarify the distinction between residue conservation and phosphorylation conservation (text file with track changes, line 618)

1.6. Regarding the evolutionary conservation of cryptic sites, have the authors taken into consideration that tyrosine-specific kinases, phosphatases, and reader domains first appeared in the first metazoans, and are for the most part not seen in non-metazoan eukaryotes? I notice some of the proteomes used for the conservation analysis include plants and yeast, which lack most tyrosine phosphorylation.

We thank the reviewer for this insightful comment. In response to the suggestion, we have recalculated the entropic conservation score by restricting the analysis to metazoan species. This analysis ensures that the evolutionary context more accurately reflects the presence and functional relevance of tyrosine-specific kinases, phosphatases, and reader domains. The comparison between the entropic score distribution calculated by including or not non-metazoan orthologues show statistically significant differences for both serine and threonine, and tyrosine. However, the large sample sizes translate inevitably into statistically significant p-values, even when the differences in mean are minimal and the standard deviations relatively small. To better assess the practical relevance of these differences, we calculated Cohen's d as a measure of effect size (Table R1). The coefficient helps assess the size and biological significance of a difference (>0.2 = small effect; >0.5 = medium effect; >0.8 = large effect). The analysis indicates a very modest deviation in entropic scores by including or not non-metazoan orthologues.

1.7. I find the argument that phosphorylation of exposed core residues is part of normal protein quality control/proteostasis to be convincing. Can the authors provide any experimental evidence to support this model (for example, greater phosphorylation of cryptic sites under stress conditions)? I don't think these experiments are necessary, but would seem to be a logical next step and could be done quite easily through collaboration.

We appreciate the reviewer's suggestion and fully agree that showing more significant phosphorylation of cryptic sites under stress conditions could represent an exciting future direction. We are conducting experiments on individual tumor suppressors such as p53 and PTEN, which harbor cryptic phosphosites, to test whether cellular stress conditions enhance phosphorylation at these positions. These studies assess whether such modifications contribute to altered protein stability or function in stress or disease contexts, particularly cancer. We plan to communicate these results in forthcoming publications and are currently open to collaborations to broaden this line of investigation.

1.8. The authors note at the end of the discussion that targeting cryptic phosphosites might be a strategy to selectively degrade some proteins in cancer. Practically, how would this work? I can't think of how, but perhaps the authors can provide more specific suggestions.

We thank the reviewer for raising this important point. One promising approach to therapeutically exploit cryptic phosphosites builds on the PPI-FIT principles (Pharmacological Protein Inactivation by Folding Intermediate Targeting). This strategy targets transient structural pockets appearing only in folding intermediates (Spagnolli et al., Comm Biology 2021). In this context, kinases that phosphorylate cryptic sites could be modulated, either inhibited or redirected, so that misfolded or oncogenic proteins are selectively marked for degradation. For example, selectively enhancing the phosphorylation of a cryptic site on an oncogenic protein could destabilize it and promote its degradation via the proteasome. Conversely, preventing phosphorylation at a cryptic site on a tumor suppressor (e.g., by inhibiting the specific kinase) could enhance protein stability and restore function. While this concept is still emerging, it offers an exciting therapeutic avenue that complements our findings. We added a paragraph addressing this point in the discussion section of the new version of the manuscript (text file with track changes, line 716).

1.9. Introduction: "It involves the addition of a phosphate to an hydroxyl group found in the side chain of specific amino acids, typically serine, threonine or tyrosine residues." Of course serine, threonine, and tyrosine are the only standard amino acids with a simple hydroxyl group, so "typically" is not needed here.

We have removed the word "typically" to reflect the accurate chemical specificity of phosphorylation events (text file with track changes, line 82).

1.10. In my view this is an important study, bringing rigor and a broad proteomic perspective to a phenomenon that (to my knowledge) had not been carefully examined previously. In terms of the big picture, I am of two minds. On the one hand, showing that phosphorylation of hydrophobic core residues exposed during translation or the early stages of folding can regulate steady state levels of some proteins provides an intriguing new mechanism to control the complement of proteins in the cell, and is potentially an area of regulation in normal physiology or in disease. On the other hand, if this is just part of the normal proteostatic mechanisms (hydrophobic core residues exposed for too long consign the protein to degradation, before it can lead to aggregation and other problems), that is a little less interesting to me. I think future work to tease out whether this mechanism is actually regulated and used by the cell to transmit information will be key. But the first step is showing that the phenomenon is real and widespread, and in my view this preprint accomplishes that goal very well.

We appreciate the reviewer's thoughtful summary and agree that distinguishing between passive proteostatic clearance and active regulatory function is essential. Toward this goal, we plan to carry out a phosphoproteomic analysis of ribosome-associated nascent chains. By mapping phosphorylation events during translation, we aim to validate our cryptic phosphosite dataset in a co-translational context and potentially identify novel regulatory modifications. This approach will also help us assess whether phosphorylation at cryptic sites is modulated context-dependently, thereby supporting a role in regulated protein expression rather than solely quality control.

2.1. Evolutionary comparison whether cryptic and non-cryptic sites are differently conserved. Two distinct distributions for cryptic and non-cryptic phospho-sites are observed and Figure 6 shows two entropy distributions of cryptic v non-cryptic. Here it is unclear whether this is significant given the different distributions of the two types when non modified.

We thank the reviewer for raising this critical point. Due to the large sample sizes in our analysis, statistical tests inevitably yield very low p-values, even when differences in mean are minimal and the standard deviations relatively small. To better assess the practical relevance of these differences, we calculated Cohen's d as a measure of effect size (Table R2). The comparison between cryptic and non-cryptic phosphosites yielded an effect size (Cohen's d = 0.4028) slightly lower than the one obtained for residues lying within protein cores or exposed on protein surfaces (Cohen's d = 0.5126), both indicating a modest but meaningful shift in entropic scores. In contrast, the comparisons between cryptic phosphosites and all core residues, as well as non-cryptic phosphosites and all surface residues, showed negligible effect sizes (Cohen's d = 0.0245 and 0.1326, respectively). These findings suggest that while statistical significance is achieved in all cases, only the difference between cryptic and non-cryptic phosphosites, or core and surface residues, reflects a meaningful biological signal. We have now included these data in the new version of the manuscript (text file with track changes, line 544).

2.2. The identification of buried modification sites and what the biological meaning / implications are is a very interesting topic. However PTM distribution on proteins is very skewed (many papers have identified ____clusters, hot spots, structural dependencies etc...) and therefore comparing modified sites on different residues and in different protein regions and with non-modified residues has to be very stringently controlled.

We fully agree with the reviewer that PTM distribution is non-random and influenced by structural and functional constraints, making comparative analyses challenging. To ensure rigor, we implemented a robust computational pipeline. Unlike other PTMs found almost exclusively on solvent-exposed residues, phosphorylation uniquely showed a distinct subset of sites with extremely low solvent accessibility. This pattern held even after applying stringent structural and dynamical filters. Specifically, we excluded low-confidence residues, small or unstructured domains, and sites that become exposed due to thermal fluctuations, using the SPECTRUS-based dynamic analysis. While we cannot entirely rule out context-specific exposure in fully folded proteins (e.g., during protein-protein interactions), we validated selected cryptic sites experimentally, and our findings were consistent with the computational predictions. We believe this multilayered approach strengthens the reliability of our classification and distinguishes cryptic phosphosites from the broader PTM landscape.

2.3. Very basic question: How do you assessed the RSA value of the residues from the alphafold structure. If it is sequence based, then it is unclear what the alpha fold structure actually contributes in this step? Although I assume it is structure based, it is not well described, only a reference.

We calculated the RSA values using the Shrake-Rupley algorithm implemented in the MDTraj Python library. This is a structure-based metric: for each PTM-carrying residue, we evaluated the absolute SASA from the 3D AlphaFold structure and normalized it against the theoretical maximum exposure for that residue in a Gly-X-Gly tripeptide, as defined in Tien et al. (2013). Thus, AlphaFold structures directly provide the atomic coordinates necessary for solvent accessibility estimation. We have now revised the Methods section to describe this process more explicitly (text file with track changes, lines 110 and 113).

2.4. Given that the different residues S,T,Y but also K for glycosylations etc. have a very different baseline RSA distribution, the distributions of modified residues as such are not so informative. Are the distributions of residues with the alpha fold LOD 0.65 different between modified and non-modified?

2.5. Same point: it is very clear that "tyrosine presenting a larger proportion of cryptic phosphor-sites", as they mainly are within folded domains to begin with. The pattern of phosphorylation and clustering is very different between the modified amino acid residue T,S,Y and needs consideration, given the large number of PTMs, a simple distribution is not sufficient to argue.

As already discussed in point 1.2 above, and correctly noted also by this reviewer, tyrosine residues are generally enriched in the hydrophobic cores of proteins, which is reflected by their typically low RSA, regardless of phosphorylation status. This tendency likely arises from the bulky and partially hydrophobic nature of the tyrosine side chain. To address the reviewer's question, we compared the RSA distributions of phosphorylated tyrosine, serine, and threonine residues with those of all these amino acids in the human proteome. We found that phosphorylated residues consistently exhibit higher RSA values than the overall averages for their respective amino acids. This is expected, as phosphorylation within protein cores would likely be destabilizing. Indeed, the existence of low-RSA phosphorylated residues, represents a significant deviation from the intrinsic tendency of tyrosine, serine, and threonine residues and suggests that cryptic sites may become accessible only transiently along protein folding pathways.

2.6. Figure 3E (proteins need names in the figure ): the cryptic site T222 (Chk1) is not in the quasi ridged domain, it is in a light color region. What is actually the SPECTRUS cutoff? The Pidc is only one sentence in the main text? It says fewer than 80% intradomain contacts in rigid domains i.e. >0.8, right, but is the domain rigid?

We have revised the original figure in the new version of the manuscript to include protein names, and clarified the domain assignments. The cryptic phosphosite T222 in Chk1 lies within a quasi-rigid domain, as identified by SPECTRUS. The color of the image does not reflect any structural property but instead it is used to distinguish different quasi-rigid domains. In particular, black regions identify unstructured domains, whereas shadows from dark grey to white identify quasi rigid domains. We apologize for the lack of clarity. We have corrected the figure legend accordingly (text file with track changes, line 912).

There is no cutoff in SPECTRUS' identification of quasi-rigid domain. Non quasi-rigid domains are simply regions of the protein that SPECTRUS cannot process properly. Meaning regions that, due to the large degree of intrinsic fluctuations, cannot be modelled as quasi-rigid.

We also expanded the description of Pidc in the main text to clarify that it quantifies the proportion of intra-domain contacts made by the phosphosite's side chain, and that a cutoff of {greater than or equal to}0.8 was used to retain only residues well-integrated within rigid domains (text file with track changes, line 243).

We hope these updates will resolve the ambiguities noted and more clearly define the criteria used in our filtering pipeline.

2.7. The evolutionary comparison (which is not my core expertise), seems again like comparing different things. Why not comparing cryptic and non-cryptic sites in the same protein regions? Also p-Y are, evolutionarily speaking, very different to p-S and p-T. How is this possibly considered in one distribution. p-Y analysis needs to be separated from the p-T and p-S analyses here.

We want to clarify that our evolutionary analyses compare residues at the aligned positions in orthologous proteins across multiple species. This approach ensures that each cryptic or non-cryptic phosphosites is assessed in its native structural and sequence context. Therefore, the comparison is not between different regions but evaluates the evolutionary conservation of specific sites across species, allowing for a direct and meaningful comparison of cryptic and non-cryptic phosphosites. In order to address the second point, we report below the entropic score distributions for serine/threonine and tyrosine, separately (Figure R5).

2.8. Have the authors thought of randomization of their data to see whether the distributions are significant?

We are unsure we fully understand what the referee means by randomizing the data in this case.

However, according to the mathematical definition of entropic score, the limit case in which, within each orthogroup, the phosphorylated amino acid is replaced by a completely random residue yields an entropic score of 1. The opposite limit, in which all members of the orthogroups have the same amino acid in the position of the phosphorylated amino acid, yields an ES of 0. We have added a paragraph in the methods to stress this point (text file with track changes, line 354).

2.9. Labeling in Suppl Figures is insufficient. E.g. In S6 what are the various WT, A and D numbering, are this independent stable transfections/clones? Figure S7 what is R? Thank you for pointing this out. We have now corrected the missing information in the revised version of the manuscript (text file with track changes, from line 992 to 1008)

2.10. Whether or not findings are "impressive" should be up to the reader, please remove these attributes in the text.

We agree with the reviewer's suggestion. We have removed subjective language such as "impressive" from the revised manuscript to ensure an objective and neutral tone, allowing readers to independently evaluate the significance of our findings (text file with track changes, line 454).

3.1. Residues with pLDDT scores below 65 were excluded from the analysis. The high-confidence measure applies to individual residues, regardless of whether the domains they belong to are also predicted with high confidence. Identifying the number of domains containing PTMs with overall high-confidence predictions could provide better insights into the orientation of modified residues within domain structures. To assess the relationship between residue-specific confidence and domain stability, we can analyze the correlation between high-confidence modified residues and the overall prediction accuracy of their domains. This could be quantified using the average error scores of domain residues. Additionally, using the average pLDDT score would indicate how many individual residues were predicted with high local structural confidence. In contrast, the average PAE (Predicted Aligned Error) score would provide insights into how well each residue's position is predicted relative to others within the domain, reflecting overall domain structural confidence.

Our analysis excluded residues with pLDDT scores below 65 to ensure high local confidence. While pLDDT provides residue-level structural confidence, assessing domain-wide prediction quality offers additional insights into modified residues' spatial organization and exposure. However, a domain-level interpretation is currently limited by the format of AlphaFold structural predictions. Specifically, AlphaFold does not provide Predicted Aligned Error (PAE) matrices for sequences split into overlapping fragments, a method used for proteins longer than 2,700 amino acids. These fragment predictions are only available in the downloadable AlphaFold proteome archives, not through the web interface, and lack the global alignment metrics (such as PAE) necessary for analyzing domain stability or inter-residue confidence within the domain context.

3.2. "Approximately 65% of proteins with cryptic phosphosites contained only one or two such residues, while less than 10% had five or more sites (Supp. Figure 3)." To better interpret this trend, it would be useful to analyze the total number of cryptic PTMs on proteins part of this study, including all modification types-not just phosphorylation. This would help determine whether the observed pattern is specific to phosphorylation or if it extends to other post-translational modifications as well.

To compare the occurrence of different cryptic PTMs, we extended our analysis to include all cryptic post-translational modifications annotated in PhosphoSitePlus, including phosphorylation, glycosylation, methylation, sumoylation, and ubiquitination. The approach allowed us to assess whether the observed distribution of cryptic phosphosites is unique or represents a more general feature of all cryptic PTMs. We observed extensive variation among the different PTMs in the proportion of proteins carrying 1, 2, or more of the same cryptic PTM (see Table R3). However, it must be noted that the relatively low number of cryptic PTMs, excluding phosphorylation, could make it difficult to determine whether these patterns reflect actual biological trends or are simply influenced by the sample size. We have not included these data in the new version of the manuscript, but we would be willing to add them if the editor or the reviewer advises us accordingly.

3.3. For the validation of cryptic sites, selecting domains under 200 amino acids was mentioned. However, was there also a minimum length threshold applied, similar to the filtering criteria used for false positives (less than 40 ignored)?

The 40-residue threshold was applied because protein domains that are too small cannot be reliably subdivided into quasi-rigid domains. Trying to run SPECTRUS on structures with fewer than 40 residues inevitably returns a warning, reflecting the intrinsic cooperative nature of quasi-rigid domains. In fact, entities composed of too few amino acids cannot properly arrange themselves into 3D structures and tend to be disordered. The same reasoning was applied when choosing the proteins to simulate. In particular, for the refolding simulations, we selected protein domains possessing the following properties:

1. Shorter than 200 amino acids to limit the computational demands.
2. Long enough to fold into an ordered 3-dimensional conformation reliably.
3. Have an experimentally determined NMR or X-ray crystal structure 3.4. To test their hypothesis that phosphorylation affects protein expression, they selected candidates for serine and threonine but excluded tyrosine. What were the reasons for not including tyrosine-related PTMs in their analysis?

Our experimental assays relied on phosphomimetic substitutions to mimic the effect of phosphorylation. While serine/threonine phosphorylation can be reasonably mimicked by E or D substitutions, there is no reliable single-residue mimic for phosphotyrosine. Indeed, E or D substitutions do not recapitulate the structural or electronic features of pTyr. Given these limitations, we excluded tyrosine phosphosites from experimental validation to avoid generating inconclusive or misleading data.

3.5. Do we know that the regulatory role of S300 on PYST1 is associated with the dual specificity of the phosphatase, and is this why it was selected as a negative regulator? While the regulatory roles of the other analyzed phosphosites on SMAD and CHK1 are discussed, there is limited mention of the specific role of S300 on PYST1 within the scope of the study.

S300 of PYST1 was selected not due to known regulatory relevance, but for technical convenience. PYST1 is a relatively small protein, facilitating computational simulations. We also had suitable reagents for detection (i.e., expression vector), and importantly, S300 was identified as a false-positive cryptic phosphosite removed by our dynamic filtering. It was a practical and structurally matched negative control for validating our computational pipeline.

3.6. When comparing the entropic scores between cryptic and non-cryptic residues, the medians are 0.43 and 0.52, respectively. Although this difference is not very high, they do observe that cryptic residues have lower scores than non-cryptic ones. The distributions also show greater overlap (Figure 6). I'm wondering if any statistical testing would help assess how distinct these two groups really are.

We thank the reviewer for the comment raised by reviewer #2, for which we provide an answer above. Briefly, given our large sample sizes, statistical tests often yield very low p-values even for minor differences. To assess the biological significance, we calculated Cohen's d (Table R2 above). The effect size between cryptic and non-cryptic phosphosites (d = 0.4028) was modest but meaningful, and slightly lower than between core and surface residues (d = 0.5126).

3.7. Why did the authors choose to rely on AlphaFold data instead of examining PDB structures? I didn't see any explanation or rationale provided for preferring AlphaFold predictions over experimentally determined structures from the PDB.

We appreciate the value of this comment. We focused on AlphaFold to maximize proteome-wide coverage. Indeed, although PDB structures offer experimentally validated conformations, their sparse and uneven proteome coverage (particularly for membrane proteins, low-abundance factors, and intrinsically disordered regions) precludes a truly global analysis. AlphaFold2 models, by contrast, deliver accurate, full-length structures for nearly the entire human proteome, enabling unbiased, large-scale mapping of cryptic phosphosites. Nonetheless, we performed the same analysis using high-resolution structures from the Protein Data Bank (PDB). The results were fully consistent with those based on AlphaFold predictions, indicating that our findings are consistent across the two databases (see Figure R6 below).

3.8. Novelty - The concept that cryptic site modifications can dysregulate signaling in cancer and other diseases is known, but systematically categorizing PTM sites into cryptic and non-cryptic to generate hypotheses for a wide range of identified PTMs remains an underdeveloped approach. This study establishes a framework for classifying PTMs based on their structural accessibility, integrating AlphaFold predictions, molecular dynamics simulations, solvent accessibility analysis, and phylogenetic conservation metrics. This approach not only enhances our understanding of PTM-mediated regulatory mechanisms but also provides a foundation for exploring how cryptic modifications contribute to protein function, stability, and disease progression.

We appreciate the reviewer's comment. To our knowledge, this is the first study to introduce and define "cryptic phosphosites" as a structurally distinct and functionally relevant subset of phosphorylation sites. While some individual cases of buried amino acids influencing cancer-related proteins have been reported, no previous study has systematically mapped, filtered, and analyzed these sites across the human proteome using integrated structural, dynamical, evolutionary, and experimental criteria.

3.9. The study relies primarily on predicted protein structures (e.g., AlphaFold), without exploring experimentally derived structures, which could provide more accurate and physiologically relevant insights.

We have addressed this point above (see reply to #3.7).

3.10. While the research demonstrates the impact of cryptic PTMs on protein function, it would be valuable to also investigate non-cryptic sites from their annotated data. By examining the effects of modifications on these non-cryptic sites, the study could further validate the importance of the cryptic versus non-cryptic classifications and help clarify the functional relevance of both types of sites.

We thank the referee for this thoughtful suggestion. We compared the proportion of cryptic or non-cryptic phosphosites associated with cancer- and disease-related mutations in each group from the COSMIC and PTMVar datasets. The percentage of phosphosites associated with the two repositories is essentially the same for cryptic and non-cryptic sites. This observation suggests that, despite their different structural and regulatory features, both site types occur similarly in disease contexts (see Table R4). We have included these data in the new version of the manuscript (text file with track changes, line 1067; and new Supp. Table 3).

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Referee #3

Evidence, reproducibility and clarity

Summary

The methods applied in this study were thoughtfully designed. The study's goals and the experiments performed to test several of their hypotheses were meticulously planned, ensuring that the research approach was robust and aligned with the objectives. The experimental design effectively addressed the key questions and provided reliable insights into the role of cryptic PTMs in protein function and disease mechanisms.

This study investigates cryptic post-translational modification (PTM) sites in the human proteome and their role in protein folding and expression, with significant implications for disease mechanisms. This work seeks to bridge the gap between the abundance of identified PTM sites and their regulatory roles in signaling pathways. A key focus of the study is on intermediate protein conformations-states that exist between fully folded and unfolded structures to determine whether these transient states contribute to disease by affecting protein synthesis, activity, stability, and degradation. To classify PTM sites as cryptic or non-cryptic, the authors used AlphaFold-predicted structures and relative solvent accessibility (RSA) scores, excluding those within quasi-rigid domain interfaces. This enabled them to create a database of mapped PTM sites, distinguishing based on their cryptic nature. Their analysis revealed that most PTMs occur at solvent-exposed residues, but unexpectedly, one-third of tyrosine phosphosites were cryptic. To assess the impact of cryptic phosphorylation on protein expression, they performed molecular dynamics (MD) simulations on SMAD and CHK1 phosphsites, showing that cryptic sites can become transiently exposed during protein folding. Their computational simulations further supported the finding that this exposure enhancing the chances of being modified and ultimately a potential mechanism for destabilization of its structure (due to that modification) to trigger degradation in physiological conditions. Experimentally, western blotting and protein half-life measurements confirmed that phosphomimetic substitutions affected protein expression, supporting their hypothesis that cryptic phosphorylation can influence protein stability and function. From an evolutionary and functional perspective, their phylogenetic analysis using entropy scores indicates that cryptic sites are more conserved. They also show that the cryptic PTM sites identified in this study were found to be substituted by phosphomimetic mutations in tumor-suppressor proteins, leading to dysregulation of their function and suppression of downstream signaling essential for tumor cell death. This study provides a framework for mapping cryptic PTM sites and understanding their role within intermediate protein folding states. By linking cryptic PTMs to their effects on protein stability, signaling pathways, and disease progression, the findings highlight a potential regulatory mechanism through which cryptic modifications contribute to cancer and other diseases.

Minor revisions

1. Result 1 - Residues with pLDDT scores below 65 were excluded from the analysis. The high-confidence measure applies to individual residues, regardless of whether the domains they belong to are also predicted with high confidence. Identifying the number of domains containing PTMs with overall high-confidence predictions could provide better insights into the orientation of modified residues within domain structures. To assess the relationship between residue-specific confidence and domain stability, we can analyze the correlation between high-confidence modified residues and the overall prediction accuracy of their domains. This could be quantified using the average error scores of domain residues. Additionally, using the average pLDDT score would indicate how many individual residues were predicted with high local structural confidence. In contrast, the average PAE (Predicted Aligned Error) score would provide insights into how well each residue's position is predicted relative to others within the domain, reflecting overall domain structural confidence.
2. "Approximately 65% of proteins with cryptic phosphosites contained only one or two such residues, while less than 10% had five or more sites (Supp. Figure 3)." To better interpret this trend, it would be useful to analyze the total number of cryptic PTMs on proteins part of this study, including all modification types-not just phosphorylation. This would help determine whether the observed pattern is specific to phosphorylation or if it extends to other post-translational modifications as well.
3. For the validation of cryptic sites, selecting domains under 200 amino acids was mentioned. However, was there also a minimum length threshold applied, similar to the filtering criteria used for false positives (less than 40 ignored)?
4. To test their hypothesis that phosphorylation affects protein expression, they selected candidates for serine and threonine but excluded tyrosine. What were the reasons for not including tyrosine-related PTMs in their analysis?
5. Do we know that the regulatory role of S300 on PYST1 is associated with the dual specificity of the phosphatase, and is this why it was selected as a negative regulator? While the regulatory roles of the other analyzed phosphosites on SMAD and CHK1 are discussed, there is limited mention of the specific role of S300 on PYST1 within the scope of the study.
6. When comparing the entropic scores between cryptic and non-cryptic residues, the medians are 0.43 and 0.52, respectively. Although this difference is not very high, they do observe that cryptic residues have lower scores than non-cryptic ones. The distributions also show greater overlap (Figure 6). I'm wondering if any statistical testing would help assess how distinct these two groups really are.
7. Why did the authors choose to rely on AlphaFold data instead of examining PDB structures? I didn't see any explanation or rationale provided for preferring AlphaFold predictions over experimentally determined structures from the PDB.

Significance

Novelty - The concept that cryptic site modifications can dysregulate signaling in cancer and other diseases is known, but systematically categorizing PTM sites into cryptic and non-cryptic to generate hypotheses for a wide range of identified PTMs remains an underdeveloped approach. This study establishes a framework for classifying PTMs based on their structural accessibility, integrating AlphaFold predictions, molecular dynamics simulations, solvent accessibility analysis, and phylogenetic conservation metrics. This approach not only enhances our understanding of PTM-mediated regulatory mechanisms but also provides a foundation for exploring how cryptic modifications contribute to protein function, stability, and disease progression.

Strengths - This study benefits from its use of multiple validation methods and false-positive filtering, resulting in a high-confidence dataset of annotated PTM sites. The combination of computational predictions and experimental analyses strengthens the validity of their findings. This integrative approach enhances the reliability of the data and provides a comprehensive understanding of cryptic versus non-cryptic PTMs in protein regulation.

Limitations

1. The study relies primarily on predicted protein structures (e.g., AlphaFold), without exploring experimentally derived structures, which could provide more accurate and physiologically relevant insights.
2. While the research demonstrates the impact of cryptic PTMs on protein function, it would be valuable to also investigate non-cryptic sites from their annotated data. By examining the effects of modifications on these non-cryptic sites, the study could further validate the importance of the cryptic versus non-cryptic classifications and help clarify the functional relevance of both types of sites.

Audience - The broader implications of this work extend to biomedical research, drug discovery, and therapeutic development. Researchers in cell signaling and systems biology who aim to understand which modification sites are crucial for evaluating the outcomes of signaling pathways can benefit from the insights generated by this study. It provides a pathway for identifying novel drug targets and enhances our understanding of disease mechanisms, particularly in cancer and other diseases. Additionally, this work encourages and motivates computational biologists to develop more efficient methods for capturing protein folding dynamics, enabling more accurate hypotheses regarding the effects of specific PTM sites and how they influence protein function and disease progression.

My expertise lies primarily in structural biology, with a strong background in developing and utilizing bioinformatics and computational tools. While I currently have less hands-on experience with experimental techniques, my comprehensive understanding of experimental methodologies, combined with an awareness of the expected outcomes, has enabled me to effectively evaluate and interpret experimental results.

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Referee #2

Evidence, reproducibility and clarity

Review on Gasparotto et al "Mapping Cryptic Phosphorylation Sites in the Human Proteome"

Gasparotte et al assess the solvent accessibility of 87,138 post-translationally modified amino acids in the human proteome (from phosphosite plus). There initial observation is that a large fraction of modified sites are buried, a finding that is pronounced for phosphorylation but not other modifications. Their approach is using alpha fold 3D structures (0.65 cut off) and RSA prediction to get a set of buried sites. Further refinement includes the removing of low-confidence segments (such as loops, linkers, or short disordered regions) and to use SPECTRUS to identified quasi-rigid domains. The idea is that quasi rigid domains may not breathe and thus will be modified during the synthesis or folding.

They generated a final dataset of 10,606 cryptic T, S and Y phosphor-sites in 5,496 proteins and state that: "These data indicate that ~5% of all known phospho-sites are cryptic. Impressively, the number translates to ~33% of phosphorylated proteins in the human proteome presenting at least one cryptic phospho-site." They focus on S417 of the SMAD2, T382 of Chk1, known to be associated with loss of function effects or proteasomal degradation and S300 of PYST1 negative control. They stably express these proteins as phospho-mimicry or alanine substitution in HEK293. Expression levels were reduced in the phosphor-D- mutant versions and upon cycloheximide treatment a reduction of the turnover time for the phospho-D CHK1 was observed. I think we are looking a large clonal difference in the supplemental figures.

The examples are supported by MD simulations that suggest that cryptic phospho-sites can occur during the folding process and affect protein homeostasis by drastically increasing degradation rate and leading to rapid turnover; Essentially the phospho-versions show a solvent exposure. Evolutionary comparison whether cryptic and non-cryptic sites are differently conserved. Two distinct distributions for cryptic and non-cryptic phospho-sites are observed and Figure 6 shows two entropy distributions of cryptic v non-cryptic. Here it is unclear whether this is significant given the different distributions of the two types when non modified. Finally, overlay of the sites with cancer mutations lists 221 mutations in COSMIC associated with cryptic phosphosites that have been annotated as cancer-related and 138 mutations in PTMVar linked to cancer and other human pathologies. The identification of buried modification sites and what the biological meaning / implications are is a very interesting topic. However PTM distribution on proteins is very skewed (many papers have identified cluster, hot spots, structural dependencies etc...) and therefore comparing modified sites on different residues and in different protein regions and with non-modified residues has to be very stringently controlled.

Points for consideration

• Very basic question: How do you assessed the RSA value of the residues from the alphafold structure. If it is sequence based, then it is unclear what the alpha fold structure actually contributes in this step? Although I assume it is structure based, it is not well described, only a reference.
• Given that the different residues S,T,Y but also K for glycosylations etc. have a very different baseline RSA distribution, the distributions of modified residues as such are not so informative. Are the distributions of residues with the alpha fold LOD 0.65 different between modified and non-modified?
• Same point: it is very clear that "tyrosine presenting a larger proportion of cryptic phosphor-sites", as they mainly are within folded domains to begin with. The pattern of phosphorylation and clustering is very different between the modified amino acid residue T,S,Y and needs consideration, given the large number of PTMs, a simple distribution is not sufficient to argue.
• Figure 3 E (proteins need names in the figure ): the cryptic site T222 (Chk1) is not in the quasi ridged domain, it is in a light color region. What is actually the SPECTRUS cutoff? The Pidc is only one sentence in the main text? It says fewer than 80% intradomain contacts in rigid domains i.e. >0.8, right, but is the domain rigid?
• The evolutionary comparison (which is not my core expertise), seems again like comparing different things. Why not comparing cryptic and non-cryptic sites in the same protein regions? Also p-Y are, evolutionarily speaking, very different to p-S and p-T. How is this possibly considered in one distribution. p-Y analysis needs to be separated from the p-T and p-S analyses here.
• Have the authors thought of randomization of their data to see whether the distributions are significant?
• Labeling in Suppl Figures is insufficient. E.g. In S6 what are the various WT, A and D numbering, are this independent stable transfections/clones? Figure S7 what is R?
• Whether or not findings are "impressive" should be up to the reader, please remove these attributes in the text.

Significance

The identification of buried modification sites and what the biological meaning / implications are is a very interesting topic. However PTM distribution on proteins is very skewed (many papers have identified cluster, hot spots, structural dependencies etc...) and therefore comparing modified sites on different residues and in different protein regions and with non-modified residues has to be very stringently controlled.

main conclusion: 5% of all known phospho-sites are cryptic, at least one in 1/3 of structured protein regions.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This preprint uses bioinformatic and experimental approaches to explore the prevalence and consequences of the phosphorylation of residues normally buried in the hydrophobic core of proteins. By cross-referencing validated human phosphosites (PhosphositePlus) with the predicted 3D structures of the human proteome (from the AlphaFold predicted protein structure database), they identified potential "cryptic" phosphosites not expected to be solvent-accessible. They further refined the list using a variety of tools and conclude that a significant percentage (roughly 25%) of known phosphosites in folded domains are cryptic. They go on to experimentally test the consequences of mutating several of these sites in known proteins either to non-phosphorylateable or phospho-mimetic residues, and found that the phosphomimetic mutants had lower half-lives and average expression levels than either the wt or non-phosphorylatable versions. Finally, they show that putative cryptic phosphorylation sites are more highly conserved that those that are surface-accessible, and that some of these cryptic sites are found in tumor suppressor genes and that phosphomimetic mutations at these sites can be found in tumor mutation databases.

Major comments:

Overall the experimental approach is relatively straightforward, and in general the authors' interpretation of the results seems reasonable. There were several areas where I believe additional analysis or discussion might clarify the interpretation, however.

1. It would be helpful if the authors could discuss whether there is any correlation between cryptic sites and the extent of experimental validation in the Phosphosite database (e.g. those that were only identified in one or a few MS experiments). It is difficult to determine stoichiometry of phosphorylation experimentally, but can any inference be made on the extent of phosphorylation of cryptic sites vs. more conventional sites located in IDRs or on the surface of globular domains?
2. The authors note that a larger percentage of tyrosine phosphorylation sites are cryptic compared with serine/threonine sites. I assume that tyrosine itself is more highly enriched in the hydrophobic cores of proteins relative to serine or threonine, due to its bulky hydrophobic side chain. Is the increased proportion of cryptic tyrosine phosphorylation sites more, less, or the same as the proportion of tyrosine in hydrophobic cores relative to serine and threonine?
3. Fig. 5D and E: I had some trouble interpreting these figures. Indicating where the native state is in the plots would be helpful (stated in text as lower right, but a rectangle on the plot would make this more obvious). The text discusses three metastable intermediates, but what is the fourth one shown on the figures (well A, close to the native state)? This could be more explicitly explained.
4. The fact that phosphomimetic mutations of cyptic sites in SMAD2 and CHK1 lead to lower expression levels and shorter half-lives is not surprising, given the expected disruption of the hydrophobic core by introduction of a charged residue. The results certainly show that if phosphorylated, these sites would decrease expression and half-life. With respect to half-life, however, if the authors are correct and cryptic sites are predominately phosphorylated co-translationally, one would expect that the half-life curves for the wt protein would not be a simple exponential, but would instead reflect two distinct populations: those that are phosphorylated during translation, and are almost immediately degraded, and those that escape phosphorylation and have the same half-life as the non-phosphorylatable mutant. Are the actual experimental results consistent with this two-population model? If not, this would be evidence that some of these cryptic sites can be exposed post-translation, either by thermal fluctuation or biological interactions.
5. The authors make a point that cryptic phosphosites are more highly conserved than non-cryptic phosphosites, but it is not clear to me whether it is the side chain itself or its ability to be phosphorylated that is conserved. Supplemental Fig. 9, if I am interpreting it correctly, would suggest it is the residue itself and not its phosphorylation that is conserved. If so, wouldn't this suggest that phosphorylation of these cryptic sites is just an inevitable consequence of the conservation of serine, threonine, and tyrosine residues in hydrophobic core regions? If the authors have evidence that argues against this simple hypothesis, they should discuss it (e.g., cryptic phosphosites are more highly conserved in some cases than non-phosphorylated tyrosine, serine, and threonine residues that are not solvent accessible).
6. Regarding the evolutionary conservation of cryptic sites, have the authors taken into consideration that tyrosine-specific kinases, phosphatases, and reader domains first appeared in the first metazoans, and are for the most part not seen in non-metazoan eukaryotes? I notice some of the proteomes used for the conservation analysis include plants and yeast, which lack most tyrosine phosphorylation.
7. I find the argument that phosphorylation of exposed core residues is part of normal protein quality control/proteostasis to be convincing. Can the authors provide any experimental evidence to support this model (for example, greater phosphorylation of cryptic sites under stress conditions)? I don't think these experiments are necessary, but would seem to be a logical next step and could be done quite easily through collaboration.
8. The authors note at the end of the discussion that targeting cryptic phosphosites might be a strategy to selectively degrade some proteins in cancer. Practically, how would this work? I can't think of how, but perhaps the authors can provide more specific suggestions.

Minor comment:

1. Introduction: "It involves the addition of a phosphate to an hydroxyl group found in the side chain of specific amino acids, typically serine, threonine or tyrosine residues." Of course serine, threonine, and tyrosine are the only standard amino acids with a simple hydroxyl group, so "typically" is not needed here.

Significance

In my view this is an important study, bringing rigor and a broad proteomic perspective to a phenomenon that (to my knowledge) had not been carefully examined previously. In terms of the big picture, I am of two minds. On the one hand, showing that phosphorylation of hydrophobic core residues exposed during translation or the early stages of folding can regulate steady state levels of some proteins provides an intriguing new mechanism to control the complement of proteins in the cell, and is potentially an area of regulation in normal physiology or in disease. On the other hand, if this is just part of the normal proteostatic mechanisms (hydrophobic core residues exposed for too long consign the protein to degradation, before it can lead to aggregation and other problems), that is a little less interesting to me. I think future work to tease out whether this mechanism is actually regulated and used by the cell to transmit information will be key. But the first step is showing that the phenomenon is real and widespread, and in my view this preprint accomplishes that goal very well.

I come from a background of studying post-translational modifications in signaling, hence my hope that a regulatory role can be found. But even if cryptic phosphorylation turns out to be unregulated, the work provides important new insight into normal proteostasis, and therefore is a valuable contribution. I should note that I don't have extensive expertise in bioinformatic methods or the computational tools to study protein dynamics, but I assume other reviewers will critically evaluate these methods.

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Reply to the reviewers

General Statements

We sincerely thank all three reviewers for their thoughtful and constructive feedback. Your comments were invaluable in improving the clarity and quality of our work.

In this study, we revisit a previously overlooked lipophilic dye, demonstrating its utility for live-cell imaging that transport in a non-vesicular pathway and label autophagy related structures. Against the backdrop of increasing attention to membrane contact sites (MCSs), bridge-like lipid transfer proteins (BLTPs), and organelle biogenesis, we aim to propose the possibility of a reversible one-way phospholipid transfer activity that really takes place in living cells.

As Reviewer #1 noted, recent cryo-EM studies (e.g., Oikawa et al.) have highlighted the importance of lipids in autophagosome formation. And there are some existed in vitro studies. However, we believe that we have to think about the consistence of simplified in vitro reconstitution and the complex real cellular environment. In addition, to our knowledge, no studies have directly tracked lipid flow dynamics over time in living cells. We believe our work contributes to this gap by combining three interesting technical approaches: (a) R18 as a lipid-tracing dye, (b) FRAP analysis on the isolation membrane, and (c) the use of Ape1 overexpression to stall autophagosome closure, enabling us to visualize reversible lipid flow in vivo. While these techniques may not appear "fancy," we hope they offer new insights that can inspire further exploration in lipid dynamics story in a real cellular environment.

We appreciate Reviewer #2's comments on our high imaging quality and Reviewer #3's recognition of our approach as an elegant way to study lipid transfer. We have revised the manuscript accordingly and included additional explanations, figure clarifications, and planned experiments to address remaining concerns.

As two key concerns were raised repeatedly by all reviewers, we would like to address them here:

1. Regarding the concern that the evidence for reversible lipid transfer from the IM to the ER is not sufficiently strong:

We are deeply grateful to Reviewer #2 for the insightful suggestion to compare the fluorescence recovery of the adjacent bleached ER to that of the ER-IM MCS, to exclude the possibility that recovery at the ER-IM MCS originates from nearby ER rather than from the IM. Following this suggestion, we performed a quantitative analysis using unbleached ER as a background. Interestingly, in every sample, the adjacent bleached ER consistently showed a significantly lower fluorescence recovery than the ER-IM MCS. We also used the IM as a background for normalization, the difference became even more pronounced, further supporting the idea that the adjacent ER could not be the source of the recovery signal at the ER-IM MCS. These findings strengthen our conclusion that phospholipid recovery at the MCS could be derived from the IM. The updated analysis and corresponding figure panels (Figure 5K, 5L, and 5M), along with the relevant text (lines 384-396), have been revised accordingly.

Regarding the concern that the evidence for R18 transfer via Atg2 as a bridge-like lipid transfer protein is not sufficiently direct:

In addition to the evidence presented in this manuscript, we have now cited our parallel study currently under revision (Sakai et al., bioRxiv 2025.05.24.655882v1), where we provide direct evidence that Atg2 indeed functions as a bridge-like lipid transfer protein, rather than a shuttle. Importantly, we also show in that study that R18 transfer requires the bridge-like structure of Atg2. This new reference has been cited in the revised manuscript, and relevant textual explanations have been added to provide further support.

We hope that the revisions and our revision plan can address the reviewers key concerns. Please find our detailed point-by-point responses below.

Response to the Reviewer ____#____1

In their study, Hao and colleagues exploited the fluorescent fatty acid R18 to follow phospholipid (PL) transfer in vivo from the endoplasmic reticulum to the IM during autophagosome formation. Although the results are interesting, especially the retrograde transport of PLs, based on the provided data, additional control experiments are needed to firmly support the conclusions.

We sincerely thank the reviewer for the positive assessment and agree that additional controls are necessary to support our conclusion. Detailed responses and corresponding revisions are provided below.

An additional point is that the authors also study the internalization of R18 into cells and found a role of lipid flippases and oxysterol binding proteins. While this information could be useful for researchers using this dye, these analyses/findings have no specific connection with the topic of the manuscript, i.e. the PL transfer during autophagosome formation. Therefore, they must be removed.

We thank the reviewer for the thoughtful comment. We understand the concern that the R18 internalization analysis may appear peripheral to the manuscript's main focus on phospholipid transfer during autophagosome formation. However, we respectfully believe that this section is critical for establishing the mechanistic basis as this study represents the first detailed in vivo application of R18 for tracing lipid dynamics. We believe it is interesting that R18 entry is not due to chemically passive diffusion or non-specific adsorption, but occurs through a biologically regulated, non-vesicular lipid transport pathway. This mechanistic context underpins the reliability of using R18 to monitor ER-to-IM lipid transport in the autophagy pathway.

To improve clarity and coherence, we have added explanatory text in the Introduction and at the start of the Results section to explicitly link the internalization assay to the subsequent autophagy-related experiments (line 94-98, 185-187). We hope this helps guide the reader through the rationale and relevance of this part of the study.

Major points:

1) In general, the quality of the microscopy images are quite poor and this make it difficult to assert some of the authors' conclusions.

We thank the reviewer for the feedback. To better address this concern, we would appreciate clarification regarding which specific images or figure panels were found to be of low quality. Overall, we believe the microscopy data presented are of sufficient resolution and clarity to support our main conclusions, as also noted by Reviewer #2 ("the high-quality images and FRAP experiments").

We acknowledge that certain phenomena-such as occasional R18 labeling of the vacuole-were not clearly explained in the original manuscript. We have now included additional clarification in the results section and mentioned this limitation in the discussion (lines 170-171, 436-438), along with a note on ongoing experiments to further investigate this point.

2) It would be important to perform some lipidomics analysis to determine in which PLs and other lipids or lipid intermediates R18 is incorporated. First, it will be important to know which the major PL species are are labelled under the conditions of the experiments done in this study. Second, the authors assume that all the R18 is exclusively incorporated into PLs and this is what they follow in their in vivo experiments. What about acyl-CoA, which has been shown to be a key player in the IM elongation (Graef lab, Cell)?

We thank the reviewer for raising this point. However, we believe this is based on a misunderstanding of the chemical nature of R18. R18 is not a free fatty acid analog and cannot be incorporated into phospholipids or acyl-CoA via metabolic pathways. Due to its chemical structure-a bulky rhodamine headgroup attached to a long alkyl chain-it cannot undergo enzymatic conjugation or incorporation into membrane lipids. This is why we did not pursue lipidomics analysis. Instead, we focused on characterizing the biological behavior of R18 through a range of live-cell assays, including temperature and ATP dependency, involvement of flippases, OSBP proteins, and Atg2, all of which support a regulated, non-vesicular lipid transport pathway. Additionally, the AF3 structural model presented in this study is consistent with this interpretation, showing no evidence of R18 forming chemical bonds with phospholipids.

3) Figure 1A and 1B. The authors conclude that Atg2 is involved in the lipid transfer since R18 does not localize to the PAS/ARS in the atg2KO cells. However, another possible explanation is that in those cells the IM is not formed and does not expand, and con sequetly R18 is present in low amounts not detectable by fluorescence microscopy. To support their conclusion, the authors must assess PAS-labelling with R18 in cells lacking another ATG gene in which Atg2 is still recruited to the PAS.

We thank the reviewer for this important suggestion. As noted, the absence of R18 at the PAS in atg2Δ cells may reflect a lack of membrane formation rather than impaired lipid transfer. However, in support of our interpretation, our previous work (Hirata E, Ohya Y, Suzuki K, 2017) has shown that R18 accumulates at PAS-like structures in delipidation mutants, where the IM fails to expand but Atg2 is still recruited (please refer to the attached revision plan for further details). This suggests that the presence of Atg2, rather than the mere existence of a mature IM, contributes to R18 localization.

To address this, we revised our statement to the more cautious: "R18 was undetectable at the PAS in atg2Δ cells," to avoid overinterpretation (lines 119-120). 4)

4) Figure 2. As written, the paragraph this figure seems to indicate that flippases are directly involved in the translocation of R18 from the PM to the ER. As correctly indicated by the authors, flippases flip PLs, not fatty acids. Moreover, there are no PL synthesizing at the PM and thus probably R18 is not flipped upon incorporation into PL. As a result, the relevance of flippase in R18 internalization is probably indirect. This must be explained clearly to avoid confusion/misunderstandings.

We thank the reviewer for this important clarification. We fully agree that flippases act on phospholipids, not fatty acids, and that R18 is not metabolically incorporated into phospholipids at the plasma membrane. However, our ongoing work (Rev. Figure 1) shows that R18 preferential labeling affinity for PS and PE in vivo (yeast phospholipid synthesis mutants), consistent with its flippase-dependent localization. Flippases are known to specifically flip PS and PE. While R18 itself is not enzymatically modified or incorporated into phospholipids, its membrane distribution may thus depend on the lipid environment and the activity of lipid-translocating proteins.

Preliminary data supporting this observation are included in the "Supplementary Figures for reviewer reference only" and are not part of the public submission.

5) A couple of manuscript has shown a (partial) role of Drs2 in autophagy. The authors must explain the discrepancy between their own results and what published, especially because they use the GFP-Atg8 processing assay, which is less sensitive than the Pho8delta60 used in the other studies.

We thank the reviewer for raising this important point. We are aware of prior reports implicating Drs2 in autophagy and in fact discussed this work directly with the authors during the course of our experiments, who kindly provided helpful suggestions. While our GFP-Atg8 processing assay did not show significant defects upon Drs2 deletion, strain background differences may explain this discrepancy. We also appreciate the suggestion to use the Pho8Δ60 assay and plan to include it in future experiments.

Additionally, authors should check whether the Atg2 and Atg18 proteins are present at the IM-ER membrane contact sites in the same rates after nutrient replenished than when cells are nitrogen-starved, since this complex would determine the lipid transfer dynamics at this membrane contact site.

We thank the reviewer for the helpful suggestion. We plan to perform additional experiments to monitor Atg18 localization during the nutrient replenishment assay.

6) Authors used a predicted Atg2 lipid-transfer mutant (Srinivasan et al, J Cel Biol, 2024), but not direct prove that this mutant is defective for this activity. As previously done for other Atg2/ATG2-related manuscripts (Osawa et al, Nat Struct Mol Biol, 2019; Valverde et al, J Cel Biol, 2019), this must be measure in vitro. Moreover, they do not show whether other known functions of Atg2 are unaffected when expressing this Atg2 mutant, e.g. formation of the IM-ER MCSs, Atg2 interaction with Atg9 and localization at the extremity of the IM...

We thank the reviewer for this concern. The lipid-transfer-deficient Atg2 mutant used here is based on the same structural rationale as in our recent parallel study (Sakai et al., bioRxiv 2025; https://www.biorxiv.org/content/10.1101/2025.05.24.655882v1, currently under revision). In that study, we addressed whether Atg2 indeed functions as a bridge-like lipid transfer protein, and also used R18 to directly demonstrate the lipid transfer defect of this Atg2 mutant in vivo.

We therefore believe that referencing this study provides mechanistic support for the use of this Atg2 mutant in the current manuscript. A citation and brief explanation have now been added to the revised text (line 315-316, 439-441). We also plan to perform the lipid transfer assay in vitro.

7) The mNG-Atg8 signal is not recovered in the fluorescent recovery assays. Based on the observation that R18 signal comes back after photobleaching, authors suggest that the supply of Atg8 is not required for IM expansion. This idea is opposite to data where the levels of Atg8 and deconjugation of lipidated Atg8 determines the size of the forming autophagosomes (e.g., Xie et al, Mol Biol Cell, 2008; Nair et al, Autophagy, 2012). Similar results have also been obtained in mammalian cells (Lazarou and Mizushima results in cell lacking components of the two ubiquitin-like conjugation systems). This discrepancy requires an explanation.

We thank the reviewer for pointing out this imprecise interpretation, and we sincerely apologize for the confusion it may have caused. We fully agree that Atg8 is essential for the expansion of the isolation membrane (IM), as supported by previous studies. In our FRAP data, mNG-Atg8 showed gradual recovery at the later timepoints, indicating that Atg8 can be replenished over time. The reason why R18 recovery appears much more rapid is likely due to the inherently fast lipid transfer activity of Atg2, the bridge-like lipid transport protein. In contrast, Atg8 signal recovery may have been delayed for two reasons: (1) slower recruitment kinetics to the IM, and (2) partial depletion of the available mNG-Atg8 protein pool due to photobleaching during the experiment.

We have revised the relevant paragraph in the manuscript (line 326-330) to clarify these points and avoid potential misinterpretation.

8) Although authors claim that there is a retrograde lipid transfer from the IM to the ER, based on the data, it quite difficult to extract these conclusions as they show a decrease in the lipid flow dynamics rather to an inversion of the lipid flow per se. Can the authors exclude that ER microdomains are formed at the ERES in contact with the IM, and consequently what they measure is a slow diffusion of R18-labeled lipid from other part of the ER to these ERES?

We appreciate the reviewer's insightful comment. Indeed, we are also considering the possibility that lipid-enriched microdomains may form in the ER and contribute to complex lipid dynamics at contact sites. However, direct visualization of such domains in cells remains technically challenging, this remains one of the important directions we aim to pursue in future studies. While our current data do not allow us to definitively state that all recovered lipids originate from the IM, our FRAP experiments provide indirect yet strong support for the possibility that at least a substantial portion of the recovered lipid signal in the ER derives from the IM. Moreover, following Reviewer 2's major point No.4, we performed a direct comparison of R18 fluorescence recovery between the photobleached ER-IM MCS region and the adjacent bleachedER region (Figure 5K and 5M). Interestingly, each sample consistently showed lower fluorescence recovery in the adjacent bleached ER near the ER-IM MCS (mean = 0.20), compared to the ER-IM MCS region (mean = 0.28). To further validate this observation, we also used the IM as a background reference for normalization. This analysis revealed a more significant difference, with the adjacent bleached ER near the ER-IM MCS showing a lower recovery (mean = 0.47) than the ER-IM MCS (mean = 0.80).

As the Reviewer2 pointed out, these results support our reversible lipid transfer model by demonstrating that fluorescence recovery at the ER-IM MCS is due to the signal coming from the IM, rather than from the adjacent bleached ER, which recovers more slowly and less efficiently. We have incorporated this new analysis into Figure 5, and accordingly revised the figure legend and main text (lines 384-396).

9) The retrograde PL transfer is studied in cells overexpressing Ape1, in which IM elongation is stalled. This is a non-physiological experimental setup and consequently it is unclear whether what observed applies to normal IM/autophagosomes. This event should be shown to occur in WT cells as well.

We thank the reviewer for this point. Indeed, it remains technically difficult to visualize lipid flow during normal IM expansion in vivo, as this process is rapid and transient. And to date, there are no reports directly addressing lipid flow in this process.

But the Ape1 overexpression system provides a strategic advantage by temporally extending the IM elongation phase and spatially enlarging the IM, thus offering a unique opportunity to capture membrane behavior that would otherwise be transient and difficult to resolve. Importantly, this system arrests autophagosome closure, which we leveraged to investigate the potential reversibility of phospholipid transfer in a controlled and prolonged context. Without this system, it would be exceedingly difficult for reaserchers to examine the lipid flow directionality in living cells.

Furthermore, the use of Ape1 overexpression has been widely employed in previous high-impact autophagy studies. We emphasize that our aim is to understand Atg2-mediated lipid transfer, and in this context, the Ape1 system provides a valuable and informative tool without compromising the validity of our conclusions.

10) From the images provided, it appears that R18 also labels the vacuole. The vacuole form MCSs with the IM. Can the author exclude a passage of R18 from the vacuole to the IM?

We thank the reviewer for the insightful comment. Our data suggest that R18 traffics from the plasma membrane to the ER, then to autophagy-related structures. Actually, following that, as we kown, autophagosomes will eventually reaches and fused with the vacuole. This explains the occasional weak R18 signals at the vacuole membrane, particularly in late-stage cells. We have revised the figure and clarified this point in the text to avoid oversimplification of R18 localization (lines 169-171, 426-428)

Here we also added the results of our onging work (in preparation). R18 tends to accumulate in a dot-like compartment after prolonged rapamycin treatment and incubation (Rev. Figure 2). And the vacuolar labeling of R18 correlates with the degradation status of autophagosomes, rather than reverse lipid transport from the vacuole to the IM (Rev. Figure 2). Taken together, we believe that R18 transport from the vacuole back to the IM is unlikely.

Preliminary data supporting this response are included in the "Supplementary Figures for reviewer reference only" and are not part of the public submission.

Minor points:

1) L66. One report has indicated that Vps13 may also play a role in the transfer of lipids from the ER to the IM (Graef lab, J. Cell Biol).

Thank you for pointing this out. Their excellent work also suggested that the inherent lipid transfer activity of Atg2 is required for IM expansion. We have revised the sentence (lines 67-68, 312-314) and included the appropriate citation at these two places.

2) L70. It must be indicated that IM is also called phagophore.

We have revised the sentence (line 70-71). Thank you for pointing this out.

3) L74. It is mentioned "Additionally, a hydrophobic cavity in the N-terminal region of Atg2 directly tethers Atg2 to the ER, particularly the ER exit site (ERES), which is considered a key hub for autophagosome biogenesis", but there is no experimental evidence supporting that Atg2 is involved in the tethering with the ERES.

Thank you for pointing this out. We have removed the N-terminal region part and revised the sentence accordingly (line 79-81) to avoid overstatement.

4) L90. PAS must be listed between the ARS.

We have revised the sentence (line 97-98). Thank you for pointing this out.

5) Upon deletion of ATG39 and ATG40, there is a pronounced reduction of mNG-Atg8 labelled with R18. This would suggest that these two ER-phagy receptors are required for the PL transfer from the ER to the IM, which is not the case as autophagy is mildly affected by the absence of them (e.g., Zhang et al, Autophagy, 2020).

We thank the reviewer for the important comment and agree that Atg39 and Atg40 are not required for phospholipid transfer from the ER to the IM. We have revised the text (lines 155-157). We appreciate if the reviewer could provide the DOI or PubMed ID for this paper.

6) Authors referred that "no direct evidence has been found to confirm lipid transfer at the ER-IM MCS in living cells" (lines 282-283). However, a recent paper has shown that de novo-synthesized phosphatidylcholine is incorporated from the ER to the autophagosomes and autophagic bodies (Orii et al, J Cel Biol, 2021). This reference should be mentioned in the manuscript.

Thank you for your insightful reminder. This paper beautifully demonstrated the importance of de novo-synthesized phosphatidylcholine in autophagy using electron microscopy. We have now included its citation and brief discussion in the revised manuscript (lines 74-76, 297-298). However, we respectfully note that direct observation of lipid transfer at the ER-IM MCS in living cells still remains unproven.

7) In lines 252-253, the sentence "R18 transport from the PM to the ER was partially impaired in osh1Δ osh2Δ, osh6Δ osh7Δ, and oshΔ osh4-1 cells (Figure S3). These results suggest that Osh proteins participate in transferring R18 from the PM to the ER" does not recapitulate what is observed in Fig. S3. Moreover, the Emr lab has generate a tertadeletion mutant in which the PM-ER MCSs are abolished. The authors could examine this mutant.

We thank the reviewer for this helpful comment and sincerely apologize for the lack of clarity in our original description. Our conclusion was primarily based on the partial PM accumulation of R18 observed in some osh mutant strains shown in Figure S3, which motivated us to further investigate this pathway using the OSW-1 inhibitor. We have revised the corresponding text to improve the logic and clarity of this section.

We appreciate the recommendation of the tether∆ mutant. Our preliminary tests indicate that R18 still properly labels the ER in tether∆ cells, suggesting that its localization is not due to passive diffusion at membrane contact sites, but rather involves specific transport mechanisms. As this is an initial observation, we plan to confirm the result and include it in a future revision.

Reviewer #1 (Significance (Required)):

General assistent: Strength: potential new system to monitor lipid flow Limitations: Indirect evidences and in the case of the retrograde transport of phospholipids, it could be an artefact of the employed experimental approach. Advance: Little advances because something in part already shown in vitro. No new mechanisms uncovered. Audience: Autophagy and membrane contact site fields.

We sincerely thank the reviewer for the overall evaluation. We agree that our current system offers indirect but promising evidence for lipid transfer events at ER-IM contact sites in vivo. While Atg2-mediated lipid transport has been proposed in vitro, our study adds value by (1) establishing a live-cell imaging way to monitor lipid flow in a non-vesicular transport pathway, (2) proposing a model of reversible one-way lipid transfer activity, and (3) addressing whether findings from simplified in vitro reconstitution accurately reflect the dynamics in the more complex real cellular environment.

We recognize the limitations of our current approach and plan to include additional analyses to more cautiously interpret the observed retrograde movement. Although we do not claim to identify a new mechanism, we believe our work provides an interesting framework to inspire future efforts aimed at directly probing lipid flow at membrane contact sites in vivo.

We also sincerely appreciate the reviewer's recognition of the potential value of this system for the autophagy and membrane contact site communities.

Response to the Reviewer ____#2

Non-vesicular lipid transfer plays an essential role in organelle biogenesis. Compared to vesicular lipid transfer, it is faster and more efficient to maintain proper lipid levels in organelles. In this study, Hao et al. introduced a high lipophilic dye octadecyl rhodamine B (R18), which specifically labels the ER structures and autophagy-related structures in yeast and mammalian cells. They characterised its distinct lipid entry into yeast cells via lipid flippase Neo1 and Drs2 on the plasma membrane, rather than through the endocytic pathway. They then demonstrated that R18 intracellular trafficking through plasma membrane to ER depends on "box-like" lipid transfer Osh proteins. They further looked into the "bridge-like" lipid transfer protein Atg2, using R18 as a lipid probe to track lipid transfer from ER to the isolation membrane (IM) during membrane expansion and reversible lipid transfer through IM to the ER-IM membrane contact sites (MCS) when autophagy is terminated by nutrient replenishment. The authors provide an interesting model of reversible directionality of Atg2 lipid transfer during autophagy induction and termination.

We sincerely thank the reviewer for the thoughtful and constructive summary of our work. We are grateful for the recognition of the novelty of using R18 to visualize non-vesicular lipid transfer in vivo and for highlighting the conceptual contribution of our proposed model of reversible Atg2-mediated transport during autophagy.

In response to the reviewer's valuable suggestions, we have revised key parts of the manuscript and prepared a detailed revision plan to address the specific concerns. We truly appreciate the reviewer's insights, which have been instrumental in improving the clarity of our study.

Major points:

1. Line 299-309: The FRAP assays were interesting and well performed. The authors photobleached R18 and Atg8 signal, and found R18 fluorescence recovery but not Atg8, which suggests lipid transfer occurs between ER and the IM and faster than Atg8 lipidation process during IM expansion. These results gave clear evidence that R18 can be transferred during IM expansion. The supply of Atg8 may not be not able to track within this time frame or the recovered amount of Atg8 may not be able to visualized due to the threshold limitation with confocal microcopy. This does not imply the supply of Atg8 to the IM is not required during IM expansion. This should be clarified.

We thank the reviewer for this valuable comment and fully agree that Atg8 is essential for IM expansion. We apologize for any ambiguity that may have suggested otherwise.

As pointed out, the lack of mNG-Atg8 recovery in our FRAP assay likely reflects the slower turnover of lipidated Atg8, limited observation time, and photobleaching of the existing protein pool. Notably, we observed a weak but gradual signal recovery at later time points, supporting this view. We have revised the relevant paragraph in the manuscript (line 326-330) to clarify these points and avoid potential misinterpretation.

Please clarify how the length of the IM is measured and determined in Figure 4H and Figure 5D.

We thank the reviewer for the vaulable comment. We have now clarified the method for quantifying IM length in the revised manuscript. Specifically, we modified the Statistical Analysis section of the Methods (line 642-643).

Line 336-342: The description of the results should be clarified. Based on Figure 5H, the authors observed a significant decrease in the mNG-Atg8 signal during photobleaching of the R18 signal.

We thank the reviewer for pointing out the ambiguity. We have now clarified the description in the revised manuscript. The sentence has been modified (line 360-362) as follows: "To determine whether nutrient replenishment terminates autophagy, we selectively photobleached the R18 signal and monitored the R18 (photobleached) and mNG-Atg8 (without photobleaching) signal following nutrient replenishment."

The authors photobleached ER-IM MCS and the ER region (boxed region in Figure 5J) and quantified fluorescence recovery, normalized to the IM region and an ER control. The ER control was taken from the other cell. It would be helpful to compare and analyse the fluorescence recovery of R18 in the bleached ER region near the ER-IM MCS to that in the ER-IM MCS. This would help to confirm the ER-IM MCS fluorescence recovery is due to signal coming from the IM.

We sincerely thank the reviewer for this insightful suggestion. We have now performed the suggested comparison. Interestingly, each sample consistently showed lower fluorescence recovery in the adjacent bleached ER near the ER-IM MCS (mean = 0.20), compared to the ER-IM MCS region (mean = 0.28). To further validate this observation, we also used the IM as a background reference for normalization. This analysis revealed a more significant difference, with the adjacent bleached ER near the ER-IM MCS showing a lower recovery (mean = 0.47) than the ER-IM MCS (mean = 0.80).

As the reviewer pointed out, these results support our reversible lipid transfer model by demonstrating that fluorescence recovery at the ER-IM MCS is due to the signal coming from the IM, rather than from the adjacent bleached ER, which recovers more slowly and less efficiently. We have incorporated this new analysis into Figure 5, and accordingly revised the figure legend and main text (lines 384-396). Again, we appreciate this constructive and helpful suggestion.

In figure 5K, the autophagic structure or IM labelled by R18 seems to be maintained when the mNG-Atg8 signal decreases or dissociates from the IM. Could the authors comment on that how they interpret the termination of the prolonged IM structure and IM shrinkage?

We thank the reviewer for this insightful observation. Based on our live-cell imaging, we speculate that following the initial dissociation of Atg8, the IM membrane undergoes a relatively slow disassembly process, potentially retracting toward the ER-IM MCS, which often localizes near ER exit sites (ERES). This suggests that IM shrinkage may proceed via Atg8-independent mechanisms. Although the precise pathway remains unclear, we occasionally observed vesiculation events during this phase, supporting the idea that membrane remodeling continues even in the absence of Atg8. In response to this comment, we have revised our manuscript to reflect these interpretations (line 494-496).

The author has shown that Atg2Δ and Atg2LT lipid transfer mutant impair R18 labelling of autophagic structures in Figure 4C. However, the evidence supporting that R18 fluorescence recovery at ER-IM MCS is mediated by reversible Atg2 lipid transfer is not direct. It would be helpful to clarify whether Atg2 stays on the enlarged autophagic membranes when the membrane has reached to its maximum length and no longer grows.

We thank the reviewer for this important suggestion. As noted in our response to Reviewer 1 (Major Point 8-2), clarifying whether Atg2/Atg18 remains at the ER-IM contact sites after IM expansion is indeed important for supporting the reversible lipid transfer model. We plan to monitor the localization of Atg18 during the nutrient replenishment assay.

Minor points:

1. Figure 2A "Dpm-GFP" is missing. The experiment replicates in Figure 2M should be indicated.

We thank the reviewer for pointing out these issues. The label for "Dpm-GFP" has been added in Figure 2A, and the number of experimental replicates for Figure 2M is now indicated in the figure legend.

Figure S2, the magenta panel should be "R18".

We thank the reviewer for catching this labeling error. We have corrected the magenta panel label in Figure S2 to "R18" in the revised version of the figure.

Line 341-342: "Figure 5H and 5J" should be "Figure 5H and 5I"

We thank the reviewer for pointing out this error. The citation has been corrected from "Figure 5H and 5J" to "Figure 5H and 5I" in the revised manuscript.

Please describe how the lipid docking model of Atg2 is generated.

We thank the reviewer for this question. We have added a description of the modeling approach in the Methods section of the revised manuscript (lines 640-646). We also added the configuration files of AlphaFold3 to the supplementary information.

Reviewer #2 (Significance (Required)):

Currently, lipid probes are emerging as powerful tools to understand membrane dynamics, integrity, and the lipid-mediated cellular functions. In this manuscript, the authors performed a detailed characterisation of octadecyl rhodamine B (R18) as a potential lipid probe, which specifically labels ER and autophagic membranes. They present high quality imaging data and performed FRAP experiments to monitor the membrane dynamics and investigate the lipid transfer directionality between the ER and autophagic structure. However, the evidence of Atg2-mediated reversible lipid transfer may not be direct and sufficient. The proposed reversible lipid transfer model is interesting and provides an explanation of lipid level regulation during autophagosome formation.

We sincerely thank the reviewer for the positive assessment of our work and for acknowledging the potential of R18 as a lipid probe, as well as the quality of our imaging and FRAP experiments. We are particularly grateful that the reviewer found the proposed model of reversible lipid transfer both interesting and relevant to the broader question of lipid regulation during autophagosome formation.

Regarding the reviewer's concern that the evidence for Atg2-mediated reversible lipid transfer may not be sufficiently direct, we agree this is a critical point. While technical limitations currently prevent direct visualization of lipid flow reversal at single-molecule resolution in vivo, we hope our revision plan strengthen the proposed model and better convey its biological relevance, while also acknowledging the current limitations and the need for further mechanistic work.

Response to the ____Reviewer #3

The authors address the question of how autophagic membrane seeds expand into autophagosomes. After nucleation, IMs expand in dependence of the bridge-like lipid transfer protein Atg2, which has been shown to tether the IM to the ER. Several studies have shown in vitro evidence for direct lipid transfer by Atg2 between tethered membranes, and previous evidence has shown that the hydrophobic groove of Atg2 implicated in lipid transfer is required for autophagosome biogenesis in vivo in yeast and mammalian cells.

In this manuscript, the authors take advantage of the dye R18, which they show accumulates mainly in the ER after a few minutes. They show specifically that the import of R18 into cells and transfer to the ER depends on the activity of flippases in the plasma membrane and OSPB-related lipid transporter. Using different sets of FRAT experiments, the authors track the fluorescence recovery of R18 in the IM, the IM-ER membrane contact site and the neighboring ER. From these experiments the authors conclude that (a) R18 is transferred to IM from the ER when IMs expand and (b) can be transferred from IMs back to the ER when autophagy is deactivated.

The use of a lipophilic dye to monitor lipid dynamics during IM expansion or dissolution is an elegant way to probe the mechanisms of lipid transfer across ER-IM contact sites. Quantitative in vivo data is critically needed to address this fundamental question in autophagy and contact site biology. However, the study remains limited in providing direct evidence that it is indeed the lipid transfer activity of Atg2, which underlies the R18 dynamics in IMs in vivo.

We sincerely thank the reviewer for this thoughtful and encouraging summary. We appreciate the recognition of our approach using R18 to visualize lipid dynamics at ER-IM contact sites, and agree that in vivo quantitative data are critically needed to advance our understanding of autophagic membrane expansion.

We also fully agree with the reviewer that our current study provides indirect-but conceptually informative-support for Atg2-mediated reversible one way lipid transfer. While prior in vitro studies have demonstrated the lipid transfer capability of Atg2, our goal here was to develop a live-cell system that allows the dynamic tracking of lipid flow in vivo, and to explore the possibility of reversible transport during autophagy termination. We hope our story will offer unique insights for future studies aiming to directly probe lipid transfer mechanisms in live cells.

Regarding the reviewer's concern about the lack of direct evidence that Atg2's lipid transfer activity underlies the observed R18 dynamics, we fully acknowledge this limitation. To address this point, we would like to cite our parallel study currently under revision (Sakai et al., bioRxiv 2025.05.24.655882v1), which provides additional mechanistic evidence linking R18 dynamics to the lipid transfer function of Atg2. Further details and planned revisions are described in the responses below.

Major points:

(1) The authors use R18in FRAP experiments to follow its transfer from the ER into IMs. However, whether this transfer is mediated by Atg2 via its inherent lipid transfer activity remains indirect. The only evidence that implicates Atg2 directly is the observation that a lipid transfer deficient Atg2 variant fails to support IM expansion and autophagosome biogenesis. A similar full-length Atg2 mutant has previously been shown to block autophagosome formation in Dabrowski et al. 2023 in yeast, which the authors do not cite or discuss, suggesting the inherent lipid transfer activity of Atg2 is required for IM expansion. However, aside from this experiment, the mechanisms underlying R18 transfer remain unclear and, while they likely depend on or are at least partially mediated by Atg2, they may involve alternative mechanisms including vesicle transport or continuous membrane contacts. Moreover, for the assays with stalled or dissolving IM, it is essential for the authors to test whether Atg2 is still associated with these IMs. It is quite possible that Atg2 dissociates from maximally expanded or dissolving IMs, which would make their interpretation of the data very unlikely. Thus, it will be critical to provide consistent evidence that lipid transfer from the IM to the ER is mediated by Atg2. Ideally, the authors would label IM with BFP-Atg8, R18, and Atg2-GFP and perform their in vivo analysis.

We sincerely thank the reviewer for the critical comments and valuable suggestions. To further support the link between R18 transfer and Atg2, we would like to highlight two complementary findings. As noted in our response to Reviewer 1 (Major Point 3), R18 can still label the PAS even when Atg2 is recruited but IM expansion is impaired, suggesting that R18 trafficking occurs in an Atg2-dependent manner. In addition, in our parallel study (bioRxiv, 2025.05.24.655882v1), we demonstrated that Atg2 acts as a bridge-like lipid transfer protein. Notably, when we mutated the bridge-forming region of Atg2, R18 transport to the IM was also disrupted.

We greatly appreciate the reviewer's reminder regarding the study by Dabrowski et al., 2023, which we have now cited and discussed in the revised manuscript (lines 66-68, 312-314). Their findings that the inherent lipid transfer activity of Atg2 is required for autophagosome formation in vivo strongly reinforce our model.

Regarding the possibility of vesicle transport, we consider this contribution minimal based on R18's preferential labeling of continuous membranes and its divergence from FM4-64 staining. As for the role of continuous membrane contacts, as also mentioned in our response to Reviewer 1, our preliminary tests indicate that R18 still properly labels the ER in tether∆ cells, suggesting that its localization is not due to passive diffusion at membrane contact sites, but rather involves specific transport mechanisms. As this is an initial observation, we plan to confirm the result and include it in a future revision.

We also thank the reviewer for the suggestion to monitor Atg2 localization at the dissolving IM. As similarly pointed out by two other reviewers, we plan to track Atg18 during the nutrient replenishment assay.

Finally, we appreciate the idea of triple-labeling with BFP-Atg8, R18, and Atg2-GFP. While our preliminary attempts encountered technical difficulties such as abnormal BFP-Atg8 localization and severe bleaching during long-term imaging in yeast, we plan to optimize this approach in future experiments.

(2) Given the ER forms contact sites with many organelles using bridge-like lipid transfer proteins, how do the authors explain the preferential accumulation of R18 in ARS and not in for example PM (Fmp27), mitochondria, endosomes or vacuole (Vps13)? Why should R18 specifically transferred by Atg2 and not or to a much lower rate by Fmp27 or Vps13?

We sincerely thank the reviewer for raising this insightful question. Indeed, we have carefully considered this point. Our data indicate that R18 labeling of autophagy-related structures (ARS) depends on Atg2, as demonstrated in the present manuscript and supported by our parallel study currently under revision (bioRxiv, 2025.05.24.655882v1).

We speculate that the preferential accumulation of R18 in ARS may arise from structural and contextual differences among bridge-like LTPs, such as Atg2, Vps13, and Fmp27. Although all are capable of mediating lipid transfer, these proteins differ in their membrane tethering modes, cargo specificity, and spatial regulation. For example, Atg2 localizes specifically to ER-IM contact sites during autophagosome formation, where membrane expansion requires rapid lipid supply. In contrast, Vps13 and Fmp27 may function at more stable or less dynamic contacts, where lipid turnover or probe accessibility is more limited. We have added a brief discussion of this point in the revised manuscript to reflect this important consideration (lines 439-444).

(3) Does R18 label autophagic bodies after they are formed. Could the authors add R18 after autophagic bodies have formed in atg15 or pep4 cells?

We thank the reviewer for this excellent suggestion. To address whether R18 can label autophagic bodies post-formation, we plan to perform additional experiments by adding R18 after autophagic bodies have accumulated in atg15Δ or pep4Δ cells. This will help clarify whether R18 incorporates into pre-formed autophagic bodies or requires earlier membrane dynamics for its labeling.

(4) Since Neo1- or OSBP-defective cells do not transfer R18 from the PM to the ER or other membranes, the authors should include these strains as controls for ER-dependent R18 transfer to ARSs.

We thank the reviewer for this insightful suggestion. To further validate the ER-dependency of R18 transfer to autophagy-related structures, we plan to include Neo1- and OSBP-deficient strains as additional controls.

Comments:

The authors neglect to mention or discuss important recent literature directly related to their study:

Schutter et al., Cell (2020); Orii et al., JCB (2021); Polyansky et al., EMBOJ (2022); Dabrowski et al., JCB (2023); Shatz et al., Dev Cell (2024)

We sincerely thank the reviewer for pointing out these important and highly relevant studies. We apologize for our oversight in not citing them earlier. Each of these works has provided valuable insights that are directly related to and have greatly informed our current study. We have now cited and discussed these references in appropriate sections of the revised manuscript.

Figure 1A and B: The authors need to describe how these cells were stained with R18 in the figure legend or text to help the reader to understand how these experiments were performed. Figure legends need to indicate at which time point after rapamycin treatment cells were analyzed.

Thank you for the helpful suggestion. We have now added the corresponding information to the figure legends to clarify the staining procedure and time points.

The authors need to clarify whether mNG-Atg8 colocalization with R18 was included for dot- and ring-like structures for WT cells as shown separately in 1A but not in 1B.

Thank you for the comment. The quantification in Figure 1B includes both dot- and ring-like structures of mNG-Atg8 colocalized with R18 in WT cells, as shown in Figure 1A. We have now clarified this point in the revised figure legend.

Figure 1C: The figure legend needs to describe the conditions cells were treated with and when cells were analyzed after rapamycin treatment (presumably).

Thank you for the helpful suggestion. We have now added the corresponding information to the figure legends.

Figure 1C: The authors should combine atg15 and pep4 deletions with atg2 or atg7 as controls in which autophagic bodies are not formed.

Thank you for the valuable suggestion. We plan to perform these experiments that combine atg15 and pep4 deletions with atg2 or atg7 as controls.

Figure 1E and F: R18 stains more than just the ER in the cells shown. In addition to atg39 and atg40, authors should include atg11 to inhibit all forms of selective autophagy.

Thank you very much for the insightful comment. We agree and plan to include the atg11Δ mutant to inhibit all forms of selective autophagy.

Figure S2A and B: The figures are mislabeled. Instead of FM4-64 it should say R18. In addition to the ER, in several images it is obvious to see R18 staining the vacuole membrane (for example Figure 2A 30 degrees) and others. Thus, the strong thresholding in S2 may give the reader an oversimplified view on R18 localization. This needs to be corrected.

Thank you very much for pointing this out. We have corrected the labeling error in Figure S2A and B. Regarding the observation that R18 occasionally labels the vacuole membrane, we agree with the reviewer's comment. Based on our data, we believe that this signal likely reflects autophagosomes that have reached and fused with the vacuole, as expected in the later stages of autophagy. We have clarified this point in the text to avoid oversimplification of R18 localization (lines 169-171, 426-428).

Figure 1G and H: In 1G, there are number of R18-stained patches not co-labeled by GFP-ER. What are these patches and which organelles to they represent? In 1H, given the tight association of the ER (omegasome) with forming IMs, it is difficult to discern whether R18 labels surrounding ER membrane or the IM itself. This needs to be more closely analyzed. The authors need to quantify these data similar to the yeast data.

Thank you for the suggestion. We plan to perform additional quantification and colocalization analysis to clarify the identity of R18-positive signals in 1G and 1H.

Figure 4A-C: A full-length PLT-deficient variant of Atg2 has been analyzed by Dabrowski et al, JCB 2023 in vivo. This work needs to be cited and discussed. The analysis needs to include punctate Atg8 structures for WT cells to exclude effects due to expansion defects.

Thank you for the suggestion. We have now cited and discussed the work by Dabrowski et al., JCB 2023 in the revised manuscript (lines 67-68, 312-314). In addition, we have included an analysis of punctate Atg8 structures in WT cells to address the concern regarding potential expansion defects.

Figure 4F-H: To measure the size changes in IMs, the authors would need to perform these experiments without bleaching the mNG-Atg8 signals.

We apologize for the lack of clarity. The method for measuring IM size has now been added to the revised manuscript. In Figure 4, we note that mNG-Atg8 fluorescence actually shows a slow recovery over time. This limited recovery likely reflects both the slower turnover of Atg8 and the fact that the pre-existing Atg8 pool at the IM was partially photobleached. We have now revised the main text to clarify this point and included additional explanation (line 326-330).

Figure 5C: The authors need to indicate the bleached areas in the mNG-Atg8 image for easier orientation. It looks to me that the area that the authors mark as IM-ER MCS is really the IM in proximity to the ER. Thus, if lipid transfer to the IM has ceased, I would not expect recovery here. If the IM-ER MCS area includes IM and the ER to similar extent, I would expect exactly what the authors show: IM does not recover while ER quickly recovers. On average, we would observe reduced recovery as shown in 5D.

Thank you for the helpful suggestion, and we apologize for the oversight during figure preparation. We have now clearly indicated the bleached areas in the merged image in Figure 5C for better orientation. Additionally, we have carefully re-examined the defined ER-IM MCS region and confirm that the quantified area indeed corresponds to the contact site between the ER and the IM. And double checked the measurements shown in the figure remain correct.

Figure 5L: Since mNG-Atg8 signal homogenously disappears from the IM, it is meaningless to measure size. How do the authors measure the size of something they cannot detect?

Thank you for pointing this out. We agree with the reviewer's comment and have removed the panel from the revised version accordingly.

Figure 5K: The authors need to show the whole bleached area overtime for the reader to be able to see where the recovered R18 signal might be coming from. Currently, it is impossible to discern whether the signal comes from the IM or from slow recovery from neighboring ER.

We appreciate this insightful comment. To address the concern and following the suggestion from Reviewer 2 (Major Point No.4), we have now revised the figure to include an additional measurement of fluorescence recovery in the adjacent bleached ER (Figure 5K and 5M) (lines 384-396). These results further support our reversible lipid transfer model by demonstrating that fluorescence recovery at the ER-IM MCS originates from the IM, rather than from the adjacent bleached ER, which shows slower and less efficient recovery.

We have also added time-lapse videos to the supplementary information due to space limitations in the main figure.

Reviewer #3 (Significance (Required)):

The use of a lipophilic dye to monitor lipid dynamics during IM expansion or dissolution is an elegant way to probe the mechanisms of lipid transfer across ER-IM contact sites. Quantitative in vivo data is critically needed to address this fundamental question in autophagy and contact site biology. However, the study remains limited in providing direct evidence that it is indeed the lipid transfer activity of Atg2, which underlies the R18 dynamics in IMs in vivo.

We sincerely thank the reviewer for this encouraging and thoughtful comment. We appreciate the recognition that our live-cell approach using a lipophilic dye provides a valuable framework to visualize lipid dynamics during autophagosome biogenesis. As the reviewer pointed out, quantitative in vivo evidence is critically needed in this field, and we hope our study contributes meaningfully toward that goal.

We also fully acknowledge the limitation. While our current data offer indirect evidence for Atg2-mediated lipid transfer, we would like to support this by our revision plan and also our parallel study (bioRxiv, 2025.05.24.655882v1) that shows Atg2 is indeed a bridge-like LTP and R18 transfer is lost in the bridge-structure defective strain. Together, we hope these can suggest that the lipid transfer activity of Atg2 underlies the observed R18 dynamics in vivo.

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Referee #3

Evidence, reproducibility and clarity

The authors address the question of how autophagic membrane seeds expand into autophagosomes. After nucleation, IMs expand in dependence of the bridge-like lipid transfer protein Atg2, which has been shown to tether the IM to the ER. Several studies have shown in vitro evidence for direct lipid transfer by Atg2 between tethered membranes, and previous evidence has shown that the hydrophobic groove of Atg2 implicated in lipid transfer is required for autophagosome biogenesis in vivo in yeast and mammalian cells.

In this manuscript, the authors take advantage of the dye R18, which they show accumulates mainly in the ER after a few minutes. They show specifically that the import of R18 into cells and transfer to the ER depends on the activity of flippases in the plasma membrane and OSPB-related lipid transporter. Using different sets of FRAT experiments, the authors track the fluorescence recovery of R18 in the IM, the IM-ER membrane contact site and the neighboring ER. From these experiments the authors conclude that (a) R18 is transferred to IM from the ER when IMs expand and (b) can be transferred from IMs back to the ER when autophagy is deactivated.

The use of a lipophilic dye to monitor lipid dynamics during IM expansion or dissolution is an elegant way to probe the mechanisms of lipid transfer across ER-IM contact sites. Quantitative in vivo data is critically needed to address this fundamental question in autophagy and contact site biology. However, the study remains limited in providing direct evidence that it is indeed the lipid transfer activity of Atg2, which underlies the R18 dynamics in IMs in vivo.

Major points:

1. The authors use R18in FRAP experiments to follow its transfer from the ER into IMs. However, whether this transfer is mediated by Atg2 via its inherent lipid transfer activity remains indirect. The only evidence that implicates Atg2 directly is the observation that a lipid transfer deficient Atg2 variant fails to support IM expansion and autophagosome biogenesis. A similar full-length Atg2 mutant has previously been shown to block autophagosome formation in Dabrowski et al. 2023 in yeast, which the authors do not cite or discuss, suggesting the inherent lipid transfer activity of Atg2 is required for IM expansion. However, aside from this experiment, the mechanisms underlying R18 transfer remain unclear and, while they likely depend on or are at least partially mediated by Atg2, they may involve alternative mechanisms including vesicle transport or continuous membrane contacts. Moreover, for the assays with stalled or dissolving IM, it is essential for the authors to test whether Atg2 is still associated with these IMs. It is quite possible that Atg2 dissociates from maximally expanded or dissolving IMs, which would make their interpretation of the data very unlikely. Thus, it will be critical to provide consistent evidence that lipid transfer from the IM to the ER is mediated by Atg2. Ideally, the authors would label IM with BFP-Atg8, R18, and Atg2-GFP and perform their in vivo analysis.
2. Given the ER forms contact sites with many organelles using bridge-like lipid transfer proteins, how do the authors explain the preferential accumulation of R18 in ARS and not in for example PM (Fmp27), mitochondria, endosomes or vacuole (Vps13)? Why should R18 specifically transferred by Atg2 and not or to a much lower rate by Fmp27 or Vps13?
3. Does R18 label autophagic bodies after they are formed. Could the authors add R18 after autophagic bodies have formed in atg15 or pep4 cells?
4. Since Neo1- or OSBP-defective cells do not transfer R18 from the PM to the ER or other membranes, the authors should include these strains as controls for ER-dependent R18 transfer to ARSs.

Comments:

The authors neglect to mention or discuss important recent literature directly related to their study:

Schutter et al., Cell (2020); Orii et al., JCB (2021); Polyansky et al., EMBOJ (2022); Dabrowski et al., JCB (2023); Shatz et al., Dev Cell (2024)

Figure 1A and B: The authors need to describe how these cells were stained with R18 in the figure legend or text to help the reader to understand how these experiments were performed. Figure legends need to indicate at which time point after rapamycin treatment cells were analyzed.

The authors need to clarify whether mNG-Atg8 colocalization with R18 was included for dot- and ring-like structures for WT cells as shown separately in 1A but not in 1B.

Figure 1C: The figure legend needs to describe the conditions cells were treated with and when cells were analyzed after rapamycin treatment (presumably).

The authors should combine atg15 and pep4 deletions with atg2 or atg7 as controls in which autophagic bodies are not formed.

Figure 1E and F: R18 stains more than just the ER in the cells shown. In addition to atg39 and atg40, authors should include atg11 to inhibit all forms of selective autophagy.

Figure S2A and B: The figures are mislabeled. Instead of FM4-64 it should say R18. In addition to the ER, in several images it is obvious to see R18 staining the vacuole membrane (for example Figure 2A 30 degrees) and others. Thus, the strong thresholding in S2 may give the reader an oversimplified view on R18 localization. This needs to be corrected.

Figure 1G and H: In 1G, there are number of R18-stained patches not co-labeled by GFP-ER. What are these patches and which organelles to they represent? In 1H, given the tight association of the ER (omegasome) with forming IMs, it is difficult to discern whether R18 labels surrounding ER membrane or the IM itself. This needs to be more closely analyzed. The authors need to quantify these data similar to the yeast data.

Figure 4A-C: A full-length PLT-deficient variant of Atg2 has been analyzed by Dabrowski et al, JCB 2023 in vivo. This work needs to be cited and discussed. The analysis needs to include punctate Atg8 structures for WT cells to exclude effects due to expansion defects.

Figure 4F-H: To measure the size changes in IMs, the authors would need to perform these experiments without bleaching the mNG-Atg8 signals.

Figure 5C: The authors need to indicate the bleached areas in the mNG-Atg8 image for easier orientation. It looks to me that the area that the authors mark as IM-ER MCS is really the IM in proximity to the ER. Thus, if lipid transfer to the IM has ceased, I would not expect recovery here. If the IM-ER MCS area includes IM and the ER to similar extent, I would expect exactly what the authors show: IM does not recover while ER quickly recovers. On average, we would observe reduced recovery as shown in 5D.

Figure 5L: Since mNG-Atg8 signal homogenously disappears from the IM, it is meaningless to measure size. How do the authors measure the size of something they cannot detect?

Figure 5K: The authors need to show the whole bleached area overtime for the reader to be able to see where the recovered R18 signal might be coming from. Currently, it is impossible to discern whether the signal comes from the IM or from slow recovery from neighboring ER.

Significance

The use of a lipophilic dye to monitor lipid dynamics during IM expansion or dissolution is an elegant way to probe the mechanisms of lipid transfer across ER-IM contact sites. Quantitative in vivo data is critically needed to address this fundamental question in autophagy and contact site biology. However, the study remains limited in providing direct evidence that it is indeed the lipid transfer activity of Atg2, which underlies the R18 dynamics in IMs in vivo.

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

Non-vesicular lipid transfer plays an essential role in organelle biogenesis. Compared to vesicular lipid transfer, it is faster and more efficient to maintain proper lipid levels in organelles. In this study, Hao et al. introduced a high lipophilic dye octadecyl rhodamine B (R18), which specifically labels the ER structures and autophagy-related structures in yeast and mammalian cells. They characterised its distinct lipid entry into yeast cells via lipid flippase Neo1 and Drs2 on the plasma membrane, rather than through the endocytic pathway. They then demonstrated that R18 intracellular trafficking through plasma membrane to ER depends on "box-like" lipid transfer Osh proteins. They further looked into the "bridge-like" lipid transfer protein Atg2, using R18 as a lipid probe to track lipid transfer from ER to the isolation membrane (IM) during membrane expansion and reversible lipid transfer through IM to the ER-IM membrane contact sites (MCS) when autophagy is terminated by nutrient replenishment. The authors provide an interesting model of reversible directionality of Atg2 lipid transfer during autophagy induction and termination.

Major points:

1. Line 299-309: The FRAP assays were interesting and well performed. The authors photobleached R18 and Atg8 signal, and found R18 fluorescence recovery but not Atg8, which suggests lipid transfer occurs between ER and the IM and faster than Atg8 lipidation process during IM expansion. These results gave clear evidence that R18 can be transferred during IM expansion. The supply of Atg8 may not be not able to track within this time frame or the recovered amount of Atg8 may not be able to visualized due to the threshold limitation with confocal microcopy. This does not imply the supply of Atg8 to the IM is not required during IM expansion. This should be clarified.
2. Please clarify how the length of the IM is measured and determined in Figure 4H and Figure 5D.
3. Line 336-342: The description of the results should be clarified. Based on Figure 5H, the authors observed a significant decrease in the mNG-Atg8 signal during photobleaching of the R18 signal.
4. The authors photobleached ER-IM MCS and the ER region (boxed region in Figure 5J) and quantified fluorescence recovery, normalized to the IM region and an ER control. The ER control was taken from the other cell. It would be helpful to compare and analyse the fluorescence recovery of R18 in the bleached ER region near the ER-IM MCS to that in the ER-IM MCS. This would help to confirm the ER-IM MCS fluorescence recovery is due to signal coming from the IM.
5. In figure 5K, the autophagic structure or IM labelled by R18 seems to be maintained when the mNG-Atg8 signal decreases or dissociates from the IM. Could the authors comment on that how they interpret the termination of the prolonged IM structure and IM shrinkage?
6. The author has shown that Atg2Δ and Atg2LT lipid transfer mutant impair R18 labelling of autophagic structures in Figure 4C. However, the evidence supporting that R18 fluorescence recovery at ER-IM MCS is mediated by reversible Atg2 lipid transfer is not direct. It would be helpful to clarify whether Atg2 stays on the enlarged autophagic membranes when the membrane has reached to its maximum length and no longer grows.

Minor points:

1. Figure 2A "Dpm-GFP" is missing. The experiment replicates in Figure 2M should be indicated.
2. Figure S2, the magenta panel should be "R18".
3. Line 341-342: "Figure 5H and 5J" should be "Figure 5H and 5I"
4. Please describe how the lipid docking model of Atg2 is generated.

Significance

Currently, lipid probes are emerging as powerful tools to understand membrane dynamics, integrity, and the lipid-mediated cellular functions. In this manuscript, the authors performed a detailed characterisation of octadecyl rhodamine B (R18) as a potential lipid probe, which specifically labels ER and autophagic membranes. They present high quality imaging data and performed FRAP experiments to monitor the membrane dynamics and investigate the lipid transfer directionality between the ER and autophagic structure. However, the evidence of Atg2-mediated reversible lipid transfer may not be direct and sufficient. The proposed reversible lipid transfer model is interesting and provides an explanation of lipid level regulation during autophagosome formation.

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

In their study, Hao and colleagues exploited the fluorescent fatty acid R18 to follow phospholipid (PL) transfer in vivo from the endoplasmic reticulum to the IM during autophagosome formation. Although the results are interesting, especially the retrograde transport of PLs, based on the provided data, additional control experiments are needed to firmly support the conclusions. An additional point is that the authors also study the internalization of R18 into cells and found a role of lipid flippases and oxysterol binding proteins. While this information could be useful for researchers using this dye, these analyses/findings have no specific connection with the topic of the manuscript, i.e. the PL transfer during autophagosome formation. Therefore, they must be removed.

Major points:

1. In general, the quality of the microscopy images are quite poor and this make it difficult to assert some of the authors' conclusions.
2. It would be important to perform some lipidomics analysis to determine in which PLs and other lipids or lipid intermediates R18 is incorporated. First, it will be important to know which the major PL species are are labelled under the conditions of the experiments done in this study. Second, the authors assume that all the R18 is exclusively incorporated into PLs and this is what they follow in their in vivo experiments. What about acyl-CoA, which has been shown to be a key player in the IM elongation (Graef lab, Cell)?
3. Figure 1A and 1B. The authors conclude that Atg2 is involved in the lipid transfer since R18 does not localize to the PAS/ARS in the atg2KO cells. However, another possible explanation is that in those cells the IM is not formed and does not expand, and con sequetly R18 is present in low amounts not detectable by fluorescence microscopy. To support their conclusion, the authors must assess PAS-labelling with R18 in cells lacking another ATG gene in which Atg2 is still recruited to the PAS.
4. Figure 2. As written, the paragraph this figure seems to indicate that flippases are directly involved in the translocation of R18 from the PM to the ER. As correctly indicated by the authors, flippases flip PLs, not fatty acids. Moreover, there are no PL synthesizing at the PM and thus probably R18 is not flipped upon incorporation into PL. As a result, the relevance of flippase in R18 internalization is probably indirect. This must be explained clearly to avoid confusion/misunderstandings.
5. A couple of manuscript has shown a (partial) role of Drs2 in autophagy. The authors must explain the discrepancy between their own results and what published, especially because they use the GFP-Atg8 processing assay, which is less sensitive than the Pho8delta60 used in the other studies.
6. Authors used a predicted Atg2 lipid-transfer mutant (Srinivasan et al, J Cel Biol, 2024), but not direct prove that this mutant is defective for this activity. As previously done for other Atg2/ATG2-related manuscripts (Osawa et al, Nat Struct Mol Biol, 2019; Valverde et al, J Cel Biol, 2019), this must be measure in vitro. Moreover, they do not show whether other known functions of Atg2 are unaffected when expressing this Atg2 mutant, e.g. formation of the IM-ER MCSs, Atg2 interaction with Atg9 and localization at the extremity of the IM...
7. The mNG-Atg8 signal is not recovered in the fluorescent recovery assays. Based on the observation that R18 signal comes back after photobleaching, authors suggest that the supply of Atg8 is not required for IM expansion. This idea is opposite to data where the levels of Atg8 and deconjugation of lipidated Atg8 determines the size of the forming autophagosomes (e.g., Xie et al, Mol Biol Cell, 2008; Nair et al, Autophagy, 2012). Similar results have also been obtained in mammalian cells (Lazarou and Mizushima results in cell lacking components of the two ubiquitin-like conjugation systems). This discrepancy requires an explanation.
8. Although authors claim that there is a retrograde lipid transfer from the IM to the ER, based on the data, it quite difficult to extract these conclusions as they show a decrease in the lipid flow dynamics rather to an inversion of the lipid flow per se. Can the authors exclude that ER microdomains are formed at the ERES in contact with the IM, and consequently what they measure is a slow diffusion of R18-labeled lipid from other part of the ER to these ERES? Additionally, authors should check whether the Atg2 and Atg18 proteins are present at the IM-ER membrane contact sites in the same rates after nutrient replenished than when cells are nitrogen-starved, since this complex would determine the lipid transfer dynamics at this membrane contact site.
9. The retrograde PL transfer is studied in cells overexpressing Ape1, in which IM elongation is stalled. This is a non-physiological experimental setup and consequently it is unclear whether what observed applies to normal IM/autophagosomes. This event should be shown to occur in WT cells as well.
10. From the images provided, it appears that R18 also labels the vacuole. The vacuole form MCSs with the IM. Can the author exclude a passage of R18 from the vacuole to the IM?

Minor points:

1. L66. One report has indicated that Vps13 may also play a role in the transfer of lipids from the ER to the IM (Graef lab, J. Cell Biol).
2. L70. It must be indicated that IM is also called phagophore.
3. L74. It is mentioned "Additionally, a hydrophobic cavity in the N-terminal region of Atg2 directly tethers Atg2 to the ER, particularly the ER exit site (ERES), which is considered a key hub for autophagosome biogenesis", but there is no experimental evidence supporting that Atg2 is involved in the tethering with the ERES.
4. L90. PAS must be listed between the ARS.
5. Upon deletion of ATG39 and ATG40, there is a pronounced reduction of mNG-Atg8 labelled with R18. This would suggest that these two ER-phagy receptors are required for the PL transfer from the ER to the IM, which is not the case as autophagy is mildly affected by the absence of them (e.g., Zhang et al, Autophagy, 2020).
6. Authors referred that "no direct evidence has been found to confirm lipid transfer at the ER-IM MCS in living cells" (lines 282-283). However, a recent paper has shown that de novo-synthesized phosphatidylcholine is incorporated from the ER to the autophagosomes and autophagic bodies (Orii et al, J Cel Biol, 2021). This reference should be mentioned in the manuscript.
7. In lines 252-253, the sentence "R18 transport from the PM to the ER was partially impaired in osh1Δ osh2Δ, osh6Δ osh7Δ, and oshΔ osh4-1 cells (Figure S3). These results suggest that Osh proteins participate in transferring R18 from the PM to the ER" does not recapitulate what is observed in Fig. S3. Moreover, the Emr lab has generate a tertadeletion mutant in which the PM-ER MCSs are abolished. The authors could examine this mutant.

Significance

General assessment:

Strength: potential new system to monitor lipid flow Limitations: Indirect evidences and in the case of the retrograde transport of phospholipids, it could be an artefact of the employed experimental approach.

Advance: Little advances because something in part already shown in vitro. No ne mechanisms uncovered.

Audience: Autophagy and membrane contact site fields.

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Reply to the reviewers

1. General Statements [optional]

*We would like to thank all the reviewers for their positive comments and valuable feedback. In addition, we would like to address reviewer 1 query on novelty, which was not questioned by the other 2 reviewers. Our study uncovered two main aspects of hypoxia biology: first we addressed the role of NF-kappaB contribution towards the transcriptome changes in hypoxia, and second, this revealed a previously unknown aspect, that NF-kappaB is required for gene repression in hypoxia. While we know a lot about gene induction in hypoxia, much less is known about repression of genes. In times of energy preservation, gene repression is as important as gene induction. *

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2. Point-by-point description of the revisions

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

• *

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

The work from Shakir et al uses different cell line models to investigate the role of NF-kB in the transcriptional adaptation of cells to hypoxia, which is relevant. In addition, the manuscript contains a large amount of data that could be of interest and even useful for researchers in the field of hypoxia and NF-kB. However, in my opinion, there are several concerns that should be revised and additional experiments that could be included to strengthen the relevance of the work.

We thank this reviewer for their positive comments.

Specific issues: In Figure 1A, the authors examine which of the genes induced by hypoxia require NF-kB by RNA sequencing analysis of cells knocked down for specific NF-kB subunits and exposed to hypoxia for 24 hours. The knockdown is about 40-60% at the RNA level, but it would be helpful to show the effect of knockdown at the protein level.

We agree with this and have added Western blot data (Sup. Figure S1F), which shows the effects of the siRNA are much more pronounced at the protein level.

All the data regarding genes induced by hypoxia in control or NF-kB siRNA-treated cells are somewhat confusing. If I understand correctly, when the data from the three different siRNAs are crossed, only 1070 genes are upregulated and 295 are downregulated in an NF-kB-independent manner. If this is the case, I think it would be easier to use this information in Figure 2 to define the hypoxia-induced genes that are NF-kB-dependent by simply considering those induced in the control that are not in the NF-kB-independent subset (rather than repeating the integration of the data without additional explanation). If the authors do this simple analysis, are the resulting genes the same or similar? In any case, the way these numbers are obtained should be shown more clearly (i.e., a new Venn diagram showing genes up- or down-regulated in the siRNA control that are not up- or down-regulated in any of the siRNA-NF-kB treatments).

Figure 1 shows the effects on gene expression of hypoxia in control and NF-____k____B ____subunit____-depleted cells compared to normoxia control cells. Figures 1F/1G compares genes up/downregulated in hypoxia when RelA, RelB, and cRel are depleted, compared to normoxia control. Figure 1 does not display N____F-____k____B____-dependent/independent hypoxia-responsive genes____, but rather the overall effect of siRNA control and siNF-____k____B treatments in hypoxia, compared to siRNA control in normoxia. Figure 2 then defines NF-____k____B-dependent ____and independent hypoxia-responsive genes. We actually define these exactly as the reviewer suggested and agree that we should show the way these numbers are obtained more clearly. We have added the suggested Venn diagrams (Sup. Figure S2) and added extra information to the methods section (page 5 of revised manuscript). We felt it was important to show all the data upfront in Figure 1 and then integrate and focus on NF-____k____B-dependent ____hypoxia-induced genes in Figure 2.

Figure 2H shows that approximately 80% of the NF-kB-dependent genes up- or down-regulated in hypoxia were identified as RelA targets, which is statistically significant compared to RelB or cRel targets. However, what is the proportion of genes identified as RelA targets in the subset of NF-kB-independent hypoxia-induced genes? And in a randomly selected set of 500-600 genes? In my opinion, this statistical analysis should be included to demonstrate a relationship between NF-kB recruitment and hypoxia-induced upregulation (expected) and downregulation (unexpected). In this context, it is surprising that HIF consensus sites are preferentially detected in the genes that are supposed to be NF-kB dependent instead of RelA consensus.

We thank the reviewer for this question, which is really helpful. The way we have displayed the stars on the graph for Figure 2H was slightly misleading we realize now. As such, we have amended the graph. RelA, RelB, and cRel bound genes (from the ChIP atlas) are all significantly enriched within our N____F-____k____B-dependent hypoxia-responsive genes, there is no statistical testing between RelA bound vs RelB bound or cRel bound. We have also performed this analysis on the NF-____k____B____-independent hypoxia-responsive genes ____and see the same trend (Sup. Figure S5B). This indicates that the enrichment of Rel binding sites from the ChIP atlas is not specific to NF-____k____B____-dependent hypoxia-responsive genes____. We have moved Figure 2H to (Sup. Figure S5A) and amended our description of the finding. This showcases how DNA binding does not necessarily mean functionality. We have amended our description of this result and limitation of the study.

Figure 3 is just a confirmation by qPCR of the data obtained in the RNA-seq analysis, which in my opinion should be included as supplementary information. Moreover, both the effects of hypoxia and reversion by RelB siRNA are modest in several of the genes tested. The same is true for Figures 4 and 5 with very modest and variable results across cell types and genes.

We appreciate this comment; we would like to keep this as a main figure for full transparency and show validation of our RNA-sequencing results.

Figure 6 shows the effect of NF-kB knockdown on the induction of ROS in response to hypoxia. In the images provided, the effect of hypoxia is minimal in control cells, with the only clear differences shown in RelA-depleted cells.

The quantification of the IF data (Figure 6B) shows ROS induction in hypoxia which is reduced in Rel-depleted cells, with RelA depletion having the strongest effect. ROS generation in hypoxia, although counterintuitive, is well documented and used for important signalling events. We believe our data supports the previously reported levels of ROS induction (reviewed in {Alva, 2024}) in hypoxia and importantly, that NF-____k____B depletion can at least partially____ reverse this.

In 6B it is not clear what the three asterisks in the normoxia control represent (compared to the hypoxia siRNA control?). This should be clarified in the figure legend or text.

We apologize for the lack of clarity we have now added this information to the figure legend.

In the Western blot of 6C, there are no differences in the levels of SOD1 after RelA depletion. Again, there is no reason not to include the NF-kB subunits in the Western blot analysis.

We have added the Western blot analysis to this figure. We were trying to simplify it. Although depletion of RelA does not rescue the hypoxia-induced repression of SOD1, depletion of RelB does. Furthermore, cRel although not statistically significant, has a trend for the rescue of this effect, see Figure 6C-D.

Finally, regarding Figure 7, the authors mention that "we confirmed that hypoxia led to a reduction in several proteins represented in this panel (of proteins involved in oxidative phosphorylation), such as UQCRC2 and IDH1 (Figure 7A-B)". The authors cannot say this because it is not seen in the Western blot in 7A or in the quantification shown in 7B. In my personal opinion, stating something that is not even suggested in the experiments is very negative for the credibility of the whole message.

We really do not agree with this comment. We do see reductions in the levels of the proteins we mentioned. We have made the figure less complex given that some proteins are very abundant while others are not. We hope the changes are now clear and apparent. We have changed the quantification normalisation to reflect this as well and modified our description of the results, see Figure 7 and Sup. Figure S18.

In conclusion, this paper contains a large amount of relevant information, but i) non-essential data should be moved to Supplementary, ii) protein levels of relevant players need to be shown in addition to RNA, iii) minimal or undetectable differences need to be considered as no-differences, and iv) a model showing what is the interpretation of the data provided is needed to better understand the message of the paper. I mean, is it p65 or RelB binding to some of these genes leading to their activation or repression, or is it RelA or RelB inducing HIF1beta leading to NF-kB-dependent gene activation by hypoxia? If this were the case, experimental evidence that NF-kB regulates a subset of hypoxia genes through HIF1beta would make the story more understandable.

We apologise but we do not know why the reviewer mentions HIF1beta. For gene induction, there is cooperation with the HIF system in some genes but not all. The most interesting and unexpected finding is that NF-kappaB is required for gene repression in hypoxia. We have added a new figure, investigating how HDAC inhibition could reverse the repression. A mechanism known to be employed by NF-kappaB when repressing genes. We have added all the blots for NF-kB, clarified the quantification and included other approaches including a CRISPR KO cell lines for both IKKs. We hope this is now clear.

Reviewer #1 (Significance (Required)):

The work presented here is interesting but does not provide a major advance over previous publications, the main message being that a subset of hypoxia-regulated genes are NF-kB dependent. However, there is no mechanistic explanation of how this regulation is achieved and several data that are not clearly connected. A more comprehensive analysis of the data and additional experimental validation would greatly enhance the significance of the work.

We politely disagree with the reviewer. Our main finding is that NF-____k____B____ does play an important role in gene regulation in hypoxia but unexpectedly, this occurs mostly via gene repression. While there is vast knowledge on gene induction in hypoxia, gene repression, which typically does not occur directly via HIF, is virtually unknown. A previous study had identified Rest as a transcriptional repressor {PMID: 27531581} but this could only account for 20% of gene repression. Our findings reveal up to 60% of genes repressed in hypoxia require NF-____k____B____, hence this is a significant finding and a major advance over previous knowledge. Furthermore, we feel this paper is an excellent data resource for the field, as it is, to our knowledge, the first study characterising the extent to which NF-____k____B is required for hypoxia-induced gene changes, on a transcriptome-wide scale. Furthermore, we have validated this across multiple cell types and also used different approaches to investigate the role of NF-kB in the hypoxia transcriptional response. We are happy that the other reviewers agree with our novel findings.

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

In this study, the authors have interrogated the role of NF-kappaB in the cellular transcriptional response to hypoxia. While HIF is considered the master regulator of the cellular response to hypoxia, it has long been known that mutliple transcription factors also play a role both independently of HIF and through the regulation of HIF-1alpha levels. Chief amongst these is NF-kappaB, a regulator of cell death and inflammation amongst other things. While NF-kappB has been known to be activated in hypoxia through altered PhD activity, the impact of this on global gene expression has remained unclear and this study addresses this important question. Of particular interest, genes downregulated in hypoxia appear to be repressed in a NF-kappaB-dependent manner. Overall, this nice study reveals an important role for NF-kappaB in the control of the global cellular transcriptional response to hypoxia.

We thank this reviewer for their positive comments.

Reviewer #2 (Significance (Required)):

Some questions for the authors to consider with experiments or discussion: -One caveat of the current study which should be discussed is that while interesting and extensive, the analysis is restricted to cancer cell lines which have dysfunctional gene expression systems which may differ from "normal" cells. This should be discussed.

We thank the reviewer for these comments. This is indeed an important aspect, which we now expand on in the discussion section. We also took advantage of RNA-seq datasets for HUVECs (a non-transformed cell lines) in response to hypoxia (Sup. Figure S15), TNF-alpha with and without RelA depletion (Sup. Figure S16). These data support our findings that in hypoxia NF-kB is important for transcriptional repression, with some contributions to gene induction, even in a non-transformed cell system.

In the publicly available data sets analyzed, were the same hypoxic conditions used as in this study. This information should be included.

We apologize if this was not clear, the hypoxia RNA-seq studies are the same oxygen level and time (1%, 24 hours), this is in the legend of Figure 4A and Sup. Figure S9 and in Sup. Table S2. We have added this information to the main text also.

• What is known about NF-kappaB as a transcriptional repressor in other systems such as the control of cytokine or infection driven inflammation? This is briefly discussed but should be expanded. This is important as a key question in the study of hypoxia is what regulates gene repression.

We have included this in the discussion and also analysed available data in HUVECs in response to cytokine stimulation with and without RelA depletion (Sup. Figure S16). This analysis revealed equal importance of RelA for activation and repression of genes upon TNF-alpha stimulation. Around 40% of genes require RelA for their induction or repression in response to TNF-a. In the discussion we have also included other references where NF-kappaB has been found to repress genes.

NF-kappaB has previously been shown to regulate HIF-1alpha transcription. What are the effects of NF-kappaB subunit siRNAs on basal HIF-1alpha transcription? In figure 7, it appears that NF-kappaB subunit siRNA is without effect on hypoxia-induced HIF protein expression. Could this account for some of the effects of NF-kappaB depletion on the hypoxic gene signature? This point needs to be clarified in light of the data presented.

We have included data for HIF-1α RNA levels in HeLa cells with/without NF-____k____B____ depletion followed by 24 hours of hypoxia (Sup. Figure S20) and we see a small reduction (~10-20%). The reviewer is correct, there was not much effect of NF-____k____B____ depletion on HIF-1α protein levels following 24 hours hypoxia in HeLa cells. Effects of NF-kappaB depletion can be found usually with lower times of hypoxia exposure or when more than one subunit is depleted at the same time. We have added this as a discussion point in the revised manuscript.

NRF-2 is a key cellular sensor of oxidative stress in a similar way to HIF being a hypoxia sensor. The authors demonstrate using a dye that ROS are paradoxically increased in hypoxia (a more controversial finding than the authors present). It would be of interest to know if NFR-2 is induced in hypoxia as a marker of cellular oxidative stress. Similarly, it would be interesting to determine by metabolic analysis whether oxidative phosphorylation (O2 consumption) is decreased as the transcriptional signature would suggest (although the difficulty of performing metabolic analysis in hypoxia is acknowledged).

To investigate if NRF2 is induced, we performed a western blot at 0, 1, and 24 hours 1% oxygen, but didn’t see any induction of NRF2 protein levels (____Sup. Figure S17A). We also overlapped our hypoxia upregulated genes with NRF2 target genes from {PMID:24647116 and PMID: 38643749} (Sup. Figure S17B) and found limited evidence of NRF2 target genes being induced. Based on these findings, it seems that NRF2 is not being induced in hypoxia, at least not at the hypoxia level/time point we have analysed. We also agree it would be ideal to measure oxygen consumption in hypoxia, but unfortunately, we do not have the technical ability to do this at present.

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

Strengths This manuscript attempts to integrate multiple strands of data to determine the role of NFkB in hypoxia -induced gene expression. This analysis looks at multiple NFkB subunits in multiple cell lines to convincingly demonstrate that NFkB does indeed play a central role in the regulation of hypoxia-induced gene expression. This broad approach integrates new experimental data with findings from the published literature.

A significant amount of work has been performed both experimentally and bioinformatically to test experimental hypotheses.

We thank this reviewer for their positive comments.

Limitations

The main analysis in the paper involves comparing the impact of knocking down different NFkB family members in hypoxia and comparing transcriptional responses. I am surprised that the authors did not include the impact of knockdown of the NFkB family members in normoxia too. The absence of these control experiments allows us to understand the role of NFkB in hypoxia, but does not give us information as to how many of those impacts are specific/ induced in hypoxic conditions. i.e. many of the observed effects of NFkB knockdown could be due to basal suppression of NFkB target genes that happen to be hypoxia sensitive. This finding is obviously important, but it would be nice to know how many of those genes are only / preferentially regulated by NFkB in hypoxia. This would give a much deeper insight into the role of NFkB in hypoxia induced gene expression.

We agree this would have been ideal. For financial reasons we limited our analysis to hypoxia samples. We have performed qPCR analysis depleting RelA, RelB and cRel under normal oxygen conditions in HeLa (Sup. Figure S8). We find that the majority of the validated genes in HeLa cells which require____ NF-____k____B for gene changes in hypoxia, are not regulated by N____F-____k____B under normal oxygen conditions____. We have also added this limitation into our discussion section.

The broad experimental approach while a strength of the paper in many ways also has its limitations e.g. Motif analysis revealing e.g. HIF-1a binding site enrichment in RelA and RelB-dependent DEGs is correlative observation and does not prove HIF involvement in NFkB-dependent hypoxia induced gene activation. Comparing responses with responses seen in one cell type with responses that have been described in a database comprised of many studies in a variety of different cells also has some limitations. These points can be described more fully in the discussion

We agree these are mere correlations and hence a limitation and we have not formerly tested the involvement of HIF. We have included this in the discussion as suggested. For HIF binding site correlation, we do also compare to HIF ChIP-seq in HeLa cells exposed to 1% oxygen, albeit at 8 hours and not 24 hours (Sup. Figure S4).

For siRNA transfections, single oligonucleotide sequences were used for RelA, RelB and cRel. This increases the potential likelihood of 'off targets' compared to pooled oligos delivered at lower concentrations. This limitation should at least be mentioned.

We agree and have now included this as a limitation in the discussion section. We have now also included analysis using wild type and 2 different IKK____⍺____/β____ double KO CRISPR cell lines generated in the following publication {PMID: 35029639}. Out of the 9 genes we identified as NF-____k____B-dependent hypoxia upregulated genes from HeLa cell RNA-seq and validated by qPCR, which are also hypoxia-responsive in HCT116 cells (Sup. Figure S11D), 6 displayed ____NF-____k____B dependence in HCT116 cells (Sup. Figure S14). We also provide new protein data in this cell system for oxidative phosphorylation markers, which show as with the siRNA depletion, rescue of repression of these proteins when NF-____k____B is inactivated.

RNA-seq experiments are performed on n=2 data which means relatively low statistical power. How has the statistical analysis been performed on normalised counts (corresponding to 2 n- numbers) to yield statistical significance? I am not familiar with hypergeometric tests - please justify their use here.

__*We use DESeq2 for differential expression analysis and filter for effect size (> -/+ 0.58 log2 fold change) and statistical significance (FDR I am not familiar with hypergeometric tests - please justify their use here.

The hypergeometric test (equivalent to a one-sided Fisher's exact test) is routinely used to determine whether the observed overlap between two gene lists is statistically significant compared to what would be expected by chance. It is also the statistical test of choice for popular bioinformatics tools which perform over representation analysis (ORA) to see which gene sets/groups/pathways/ontologies are over-represented in a gene list, examples include Metascape, clusterProfiler, WebGestalt (used in this study), and gProfiler.

P14 RelB is described as having the most widespread impact of hypoxia dependent gene changes across all cell systems tested. Could this be due to a more potent silencing of RelB and / or due to particularly high/ low expression of RelB in these cells in general?

This is an excellent point, at the RNA level the RelB depletion is slightly more efficient (Sup. Figure S1), at the protein level, silencing is highly potent with all 3 siRNAs (Sup. Figure S1). We looked at the RNA levels of RelA, RelB and cRel in HeLa cells at basal conditions, and RelA shows the highest abundance compared to RelB and cRel, while RelB and cRel have similar expression levels (see below). However, RelB is very dynamic in response to hypoxia, something we have observed but have not published yet.

P18 For western blot analysis best practise is to have 2 MW markers per blot presented

We have and have added the second MW markers suggested.

For quantification, I suggest avoiding performing statistical analysis on semi-quantitative data unless a dynamic range of detection (with standards) has been fully established.

We agree this has many limitations, we will keep the quantification but moved into supplementary information.

P19 There is clearly an effect of reciprocal silencing with the NFkB knockdown experiments ie. siRelA affects RelB levels in hypoxia and vice versa. The implications of this for data interpretation should be discussed.

Indeed, it is well known that RelB and cRel are RelA targets. Less is known about RelA as it is not a known NF-____k____B____ target. We have added a discussion in the revised manuscript.

P20 The literature can be better cited in relation RelB and hypoxia A brief search reveals a few papers that should be mentioned/ discussed. Oliver et al. 2009 Patel et al. 2017 Riedl et al. 2021

We have looked into these suggestions. Oliver et al, refer to hypercapnia, not hypoxia and the other two only briefly mentioned RelB with no effects toward the goals of their studies. We have tried to incorporate what is currently known as much as possible.

I suggest leaving out mention of IkBa sumoylation and supplementary figure 10. I'm not sure the data in the paper as a whole merits focus on this very specific point.

We thank the reviewer for this suggestion and we have removed this aspect from the manuscript.

There is a very strong reliance on mRNA and TPM data. Some additional protein data in support of key findings will enhance

We have added additional protein level analysis where we could obtain antibodies, see Figures 6, 7 and Sup. Figures S17, S18, and S19 for our protein level analysis.

A graphical abstract summarising key findings with exemplar genes highlighted will enhance.

We have added a model to summarise our findings as suggested.

Both HIF and NFKB are ancient evolutionarily conserved pathways. Can lessons be learned from evolutionary biology as to how NFkB regulation of hypoxia induced genes occured. Does the HIF pathway pre-date the NFkB pathway or vice versa. This approach could be valuable in supporting the findings from this study.

We have investigated this. Unfortunately, there are very little available data on hypoxia gene expression in lower organisms. However, we have added a few sentences on the evolution of NF-____k____B____ and HIF.

Minor comments P2 please briefly explain how 5 genes give rise to 7 proteins

We have added this to the introduction as requested.

P2 there seems to be some recency bias in the studies cited as being associated with NFkB activation in response to hypoxia. Mention of Koong et al (1994) and Taylor et al (1999) and other early papers in the field will enhance

We have added these as suggested.

P3 The role of PHD enzymes in the regulation of NFkB in hypoxia can be introduced and / or discussed

We have added a reference to this aspect as suggested.

P8 I suggest use of proportional Venn diagrams to demonstrate the patterns more clearly

We have added these as suggested.

P11 To what extent might NFkB and Rest co-operate/ co-regulate gene repression in hypoxia?

This is a good question. We have overlapped our datasets with Rest-dependent hypoxia-regulated genes identified by Cavadas et al., (Figure below), and find that these appear to act independently of each other for the most part, with very few genes co-regulated by both.

Reviewer #3 (Significance (Required)):

Shakir et al. present a manuscript titled 'NFkB is a central regulator of hypoxia-induced gene expression'.

The research group are experts in both NFkB and hypoxia signaling and are the ideal group to perform these studies.

Hypoxia and inflammation are co-incident in many physiological and pathophysiological conditions, where the microenvironment affects disease severity and patient outcome. The cross talk between inflammatory and hypoxia signaling pathways is not fully described. Thus, this manuscript takes a novel approach to an established question and concludes clearly that NFkB is a central regulator of hypoxia-induced gene expression.

We thank the reviewer for these positive comments.