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1. General Statements

In this study, we mechanistically define a new molecular interaction linking two of the cell's major morphological regulatory pathways-the Rho GTPase and Hippo signaling networks. These two major signaling pathways are both required for life across huge swaths of the tree of life. They are required for the dynamic organization and reorganization of proteins, lipids, and genetic material that occurs in essential cellular processes such as division, motility and differentiation. For decades these pathways have been almost exclusively studied independently, however, they are known to act in concert in cancer to drive cytoskeletal remodeling and morphological changes that promote proliferation and metastasis. However, mechanistic insight into how they are coordinated is lacking.

Our data reveal a mechanistic model where coordination is mediated by the RhoA GTPase-activating protein ARHGAP18, which forms molecular interactions with both the tumor suppressor Merlin (NF2) and the transcriptional co-regulator YAP (YAP1). Using a combination of state-of-the-art super-resolution microscopy (STORM, SORA-confocal) in cultured human cells, biochemical pulldown assays with purified proteins, and analyses of tissue-derived samples, we characterize ARHGAP18's function from the molecular to the tissue level in both native and cancer model systems.

Together, these findings establish a previously unrecognized molecular connection between the RhoA and Hippo pathways and culminate in a working model that integrates our current results with prior work from our group and decades of prior studies. This model provides a new conceptual framework for understanding how RhoA and Hippo signaling are coordinated to regulate cell morphology and tumor progression in human cells.

In this substantially revised manuscript, we have addressed all comments from the expert reviewers described point-by-point below. A shared major comment from the reviewers was the request for direct evidence of the proposed mechanistic model. To address these constructive comments, we've added new experiments, new quantification, new text, new control data, and have added two expert authors, adding super-resolution mouse tissue imaging data for the endogenous study of ARHGAP18 in its native condition. We believe that these additions greatly enhance the manuscript and collectively address the overall message from the reviewer's collective comments.

2. Point-by-point description of the revisions

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

This manuscript describes a dual mechanism by which ARHGAP18 regulates the actin cytoskeleton. The authors propose that in addition to the known role for ARHGAP18 in regulating Rho GTPases, it also affects the cytoskeleton through regulation of the Hippo pathway transcriptional regulator YAP. ARHGAP18 knockout Jeg3 cells are were generated and show a clear loss of basal stress fiber like F-actin bundles. The authors further characterize the effects of ARHGAP18 knockout and overexpression. It is also discovered that ARHGAP18 binds to the Hippo pathway regulator Merlin and to YAP. Ultimately it is concluded that ARHGAP18 regulates the F-actin cytoskeleton through dual regulation of RHO GTPases and of YAP. While the phenotype of the ARHGAP18 knockout and the association of ARHGAP18 with Merlin and YAP is interesting, I found the authors conclusion that these phenotypes are due to ARHGAP18 regulation of both RHO and YAP to be based on largely correlative evidence and sometimes lacking in controls or tests for significance. In addition the authors often make overly strong conclusions based on the experimental evidence. In some instances, the rationale for how the experimental results support the conclusion is insufficiently articulated, making evaluation challenging. In general although the authors have some interesting observations, more definitive experiments with proper controls and statistical tests for significance and reproducibility are needed to justify their overall conclusions.

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*We appreciate the reviewers' constructive comments and have added substantial new data and quantifications to address their concerns. We have focused these new data on directly testing the proposed mechanisms, adding controls, and performing quantitative analysis with statistical testing. Additionally, we have edited our language to make our rationale clearer and to present our conclusions as a more moderate assessment of our experimental results. Below we respond to the specific comments made by the reviewer, followed by a list of additional editorial changes we've made based on the reviewer's overarching comments on clarity and rationale. *

Specific Comments

1) The authors make a big point about the effects of ARHGAP18 on myosin light chain phosphorylation. However, this result is not quantified and tested for statistical significance and reproducibility.

*We thank the reviewer for their comments on our western blotting quantification, which in the original submission version had quantification of RhoA downstream signaling of pCofilin/ Cofilin and pLIMK/ LIMK. We had withheld the pMLC and MLC quantification as the result was previously published with quantification, reproducibility, and statistical significance by our group in our prior manuscript on ARHGAP18 published in Elife in 2024 (Fig. 4E of *

https://doi.org/10.7554/eLife.83526 ). However, these prior results lacked the new overexpression data. We recognize the need to add these data to this manuscript as requested by the reviewer.

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*To address the reviewer's comment, we have added quantification of pMLC/MLC (Fig. 1F) *

2) Along similar lines in Figure 2C they state that overexpression of ARHGAP18 causes cells to invade over the top of their neighbors. This might be true and interesting, but only a single cell is shown and there is no quantification or controls for simply overexpressing something in that cell. The authors also conclude from this image that the overexpression phenotype is independent of its GAP activity on Rho. It is not clear how this conclusion is made based on the data. It would seem like a more definitive experiment would be to see if a similar phenotype was induced by an ARHGAP18 mutant deficient in GAP activity.

Based on the reviewer's comment, we recognize the qualitative statements made in Figure 2C (now Figure 3) should've been made more quantitative. We have added the control of Jeg 3 WT cells expressed with empty vector flag to show that WT cells do not invade over the top of each other (Fig. 3F). Additionally, we have added the quantification found in Fig. 3E, which shows the % invasive/ non-invasive cells between WT and ARHGAP18 overexpression cells. We have clarified our conclusions to make clear that these data do not directly test if the invasive phenotype derives from a Rho-independent mechanism. The text now states the following conclusion alongside others, which can be seen in our tracked changes:

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"These data support the conclusion that ARHGAP18 acts to regulate basal and junctional actin. However, it was not clear whether this activity occurred through a Rho-independent or a Rho-dependent mechanism."

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We have added new data of cells expressing an ARHGAP18 mutant deficient in GAP activity, which is explained in detail in the following response below.

3) In Figure 3 the authors compare gene expression profiles of ARHGAP18 knockout cells to wild-type cells. They see lots of differences in focal adhesion and cytoskeletal proteins and conclude that this supports their conclusion that ARHGAP18 is not just acting through RHO. The rationale for this in not clear. In addition, they observe changes in expression profiles consistent with changes in YAP activity. They conclude that the effects are direct. This very well might be true. However RHO is a potent regulator of YAP activity and the results seem quite consistent with ARHGAP18 acting through RHO to affect YAP.

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We thank the reviewer for their comment and believe the revised manuscript now presents direct evidence to support the conclusions made through the editing text and the incorporation of new data.

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First, the reviewer highlighted that we were not clear in our rationale and explanation of the conclusions made from our RNAseq data in the new Figure 4 (Previously Figure 3). We agree with the reviewer that the RNAseq data alone is not sufficient rationale for the conclusion that ARHGAP18 is acting through YAP directly. In the revised manuscript, the conclusion is now made based on the combination of our multi-faceted investigation of the relationship between ARHGAP18 and YAP (most importantly, new Figure 5). It's important for us to argue that our RNAseq analysis is much more robust and specific than simply reporting a descriptive assay seeing lots of differences in cytoskeletal proteins. We recruited an outside RNAseq expert collaborator; Dr. Yongho Bae, to perform state-of-the-art IPA analysis and a grueling manual curation of the top hit genes to identify the predominant signaling pathways linking the loss of ARHGAP18 to known YAP translational products. We've provided a supplemental table listing each citation supporting the identified YAP pathway associations from this manual curation. We also have added a new discussion paragraph on RNAseq data to clarify our specific RNAseq data results and analysis. In the revised manuscript, we have moderated our language in the results text regarding the RNAseq data to reflect the reviewer's suggestion:

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"Our RNAseq data alone could not independently confirm if the alterations to transcriptional signaling and expression of actin cytoskeleton proteins were through a Rho-dependent or Rho-independent mechanism."

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Second, in this comment and the above, the reviewer highlights the need for a new experiment to directly test the Rho Independent effects of ARHGAP18, which we now provide in the new Figure 5. In this new data, we've applied an experimental design suggested by reviewer 2 regarding the same concern. In short, we've produced and expressed a point mutant variant ARHGAP18(R365A), which abolishes the Rho GAP activity while maintaining the remainder of the protein intact. This construct allows us to directly test the effects of ARHGAP18 independent from its RhoA GAP activity. We find that the GAP-deficient ARHGAP18 is able to fully rescue basal focal adhesions, indicating that the basal actin phenotype is at least in part regulated through a Rho-independent mechanism.

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*We believe the revised manuscript, when taken in totality, provides the definitive proof requested by the reviewer. Specifically, the combination of Figure 5, where we show new data using the ARHGAP18(R365A) variant, and the result that ARHGAP18 forms a stable complex with YAP (Fig. 6G) or Merlin (Fig.6A), is supportive of direct Rho-independent molecular interactions between YAP, Merlin, and ARHGAP18. *

4) In Figure 4A showing Merlin binding to ARHGAP18 there is no control for the amount of Merlin sticking to the column as was done in Figure 4F for binding experiments with YAP. This makes it difficult to determine the significance of the observed binding.

We have performed the requested control experiment and added the results to Figure 6A.

5) The images in Figure 4C showing YAP being maintained in the nucleus more in ARHGAP18 knockout cells compared to wild-type. However the images only show a few cells and YAP localization can be highly variable depending on where you look in a field. Images with more cells and some sort of quantification would bolster this result.

We have provided quantification (Figure 6D) of what was originally Figure 4C (now Figure 6C).

Reviewer #1 (Significance (Required)):

While the phenotype of the ARHGAP18 knockout and the association of ARHGAP18 with Merlin and YAP is interesting, I found the authors conclusion that these phenotypes are due to ARHGAP18 regulation of both RHO and YAP to be based on largely correlative evidence and sometimes lacking in controls or tests for significance. In addition the authors often make overly strong conclusions based on the experimental evidence. In some instances, the rationale for how the experimental results support the conclusion is insufficiently articulated, making evaluation challenging. In general although the authors have some interesting observations, more definitive experiments with proper controls and statistical tests for significance and reproducibility are needed to justify their overall conclusions.

In the above comments, we detail the specific definitive experiments, proper controls, and statistical tests for significance, requested by the reviewer, which we believe greatly strengthen our manuscript.

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

This manuscript investigates the Rho effector, ARHGAP18 in Jegs cells, a trophoblastic cell line. It presents a number of new pieces of data, which increase our understanding of the importance of this GAP on cell function and explains at a molecular level previous results of other workers in the field. ARHGAP18 was originally given the name "conundrum' and continues to stand apart from the majority of other GAP proteins and their functions. Hence the data here is significant and of high standard.

The data is clear, and the images are of high quality and extremely impressive in their resolution. It is significant and adds a further layer to our understanding of the regulation of cell migration, particularly in the formation and resolution of microvilli.

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We appreciate the reviewer's comments and supportive insights.

The data is based on the use of the cell line Jeg3. Even the authors previous publication in eLife is based only on this cell line. They need to show the conclusions are general and not specific to this line of cells. As an extension of this, is the ARHGAP18 function shown here only in transformed cells? Does the same mechanisms operate in normal cells, which respond to activation to proliferate or migrate?

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• We respectfully point out that the critical experiments of the prior eLife publication were validated in DLD-1 colorectal cells and not Jeg-3 cells alone (Figure 1-figure supplement 2). Our newly independent lab, established just over a year ago, is unable to perform a full expansion of the manuscript using untransformed cells, however, we agree with the reviewer's perspective and wish to address the comment to the best of our current capability. To answer the reviewers' suggestions, we have recruited Dr. Christine Schaner Tooley, an expert in mouse model system studies. In the revised manuscript, we've added new Super-Resolution SORA confocal images of endogenous ARHGAP18's localization in the intact intestinal villi tissue, and apical junctions of WT mice (Fig.1A-C). These data indicate that endogenous ARHGAP18 is enriched (but not exclusively localized) at the apical plasma membranes of normal WT epithelial cells. This localization, where both Merlin and Ezrin are present at apical membrane/ junctions under normal conditions, is a major component of the working model proposed in Fig. 7. These data also indicate that ARHGAP18 is capable of entering the nucleus in WT cells, another critical aspect of our proposed model. Collectively, our DLD-1 studies published previously and or new studies using WT mice tissue samples support the conclusion that at least some of ARHGAP18's functions described in this manuscript are not limited to Jeg3 cells.*

In endothelial cells, Lovelace et al 2017 showed localization to microtubules and that depletion of ARHGAP18 resulted in microtubule instability. The authors may like to comment on the differences. Is this a cell type difference or RhoA versus RhoC difference?

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In our previous publication (Lombardo Elife), we validated the finding that ARHGAP18 forms a complex with microtubules, as we detected tubulin in the ARHGAP18 pulldown experiment (Figure 1- Source Data). However, our data indicate that in Jeg3 cells ARHGAP18 does not localize to the same microtubule associated spheres observed in the Lovelace publication. We now comment on the shared conclusions and differences between this manuscript and the Lovelace et al 2017 in the discussion section.

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"In endothelial cells, ARHGAP18 has been reported to localize microtubules and plays a role in maintaining proper microtubule stability (Lovelace et al., 2017). In our epithelial cell culture models and WT mouse intestine, we have been unable to detect ARHGAP18 at microtubules suggesting ARHGAP18 may have additional functions is various cell types."

On pages 7,9 they conclude that MLC and basal and junctional actin are regulated through a GAP independent mechanism. The best way to show this is with overexpression of a GAP mutant.

We appreciate the reviewer's insight and have produced and expressed a GAP mutant, ARHGAP18(R365A), in our cells, directly testing our conclusion that ARHGAP18 has a GAP-independent function. These data are now presented in revised Figure 5 and explained further in response to reviewer #1.

There is a huge amount of data presented in Figure 3, but their 2 genes which they focus on, LOP1 and CORO1A, are discussed but no actual data presented in support.

We now validate the CORO1A by qPCR in Figure 4J.

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Reviewer #2 (Significance (Required)):

The data is significant and adds a further layer to our understanding of the regulation of cell migration, particularly in the formation and resolution of microvilli. This manuscript will be of significance to an basic science audience in the field of RhoGTPases and cell migration.

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

The study by Murray et al explores the effects of ARHGAP18 on the actin cytoskeleton, Rho effector kinases, non-muscle myosin, and transcription. Using super resolution microscopy, they show that in ARHGAP18 KO cells there is a mixed and unexpected cytoskeleton phenotype where myosin phosphorylation appears to be increased, but actin is disorganised with reduced stress fibres, diminished focal adhesions and augmented invasiveness. They conclude that the underlying mechanisms are likely independent from RhoA. Next, they perform RNAseq using the KO cells and identify an array of dysregulated genes, including those that play crucial roles in microvilli (related to previously published findings). Analysis of the data identify gene expression changes that are relevant for altered focal adhesion (integrins). Further analysis reveals that a large cohort of the dysregulated genes are YAP targets. They then show that in ARHGAP18 KO cells YAP nuclear localization, as detected by immunostaining, is augmented; and demonstrate that immobilized ARHGAP18 protein can bind the Hippo regulator merlin as well as YAP itself.

Major comments:

1, The premise of the study (that ARHGAP18 is a RhoA effector or may acts independently of RhoA) remains not proven.

We have added new evidence of direct RhoA independent activity for ARHGAP18 described in the above comments. Specifically, we've added data using a RhoA-GAP dead variant of ARHGAP18 in Figure 5, which we believe addresses this comment.

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At several places (including in the title) the authors refer to ARHGAP18 as a Rho effector, which would suggest that it is downstream form Rho, but the basis for this is not clear. In fact, their own previous study suggested that ARHGAP is a RhoA regulator, rather than an effector. In general, the connection of the described effects to RhoA remains unclear, and not addressed in this study. The authors seem to go back and forth in their conclusions regarding the connection between ARHGAP18 and RhoA. For example, the first section of results is finished by stating (line 194): "These data support the conclusion that ARHGAP18 acts to regulate basal and junctional actin through Rho-independent mechanism". But the next section starts by stating (line 198): "We hypothesized that the invasive and cytoskeletal phenotypes observed at the basal surface of cells devoid of ARHGAP18 may be a result of changes in regulation at the transcriptional level either directly through RhoA signaling or through an additional mechanism specific to ARHGAP18". The paper would be strengthened by adding data that show whether the effects are indeed downstream, from RhoA or RhoA independent. If there is no sufficient demonstration that ARHGAP18 is downstream of RhoA and is an effector, this needs to be stated explicitly, and the wording should be changed.

*We now provide new data in Figure 5, which directly tests the RhoA independent functions of ARHGAP18 as recommended by the reviewer. Our understanding of the term effector is 'a molecule that activates, controls, or inactivates a process or action.' Based on this understanding, we used the term to convey ARHGAP18's functional role within the feedback loop, rather than to imply that it acts exclusively downstream. *

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We seek to clarify our perspective with the reviewer's assertion that we go "back and forth" as to if ARHGAP18 functions in a Rho Dependent or Rho Independent manner. It was our intent to propose a model where ARHGAP 18 acts in two separate circuits that regulate cell signaling. The first circuit involves ARHGAP18's canonical RhoA GAP activity, which involves ERMs and LOK/SLK, and is limited to the apical plasma membrane. This first signaling circuit was characterized in our prior Elife manuscript (Lombardo et al., 2024) and in an earlier JCB manuscript (Zaman and Lombardo et al., 2021). In this newly revised manuscript, we provide a partial mechanistic characterization of the second circuit, which we freely admit is much more complex and will likely require additional study to fully characterize.

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As both circuits operate as signaling feedback loops, we find the terms 'upstream' and 'downstream' to be of limited value, and we attempt to avoid their use when possible. We retain their use only when referring to the Hippo and ROCK signaling cascades, where these designations are well established. We suggest that the conceptual inconsistencies of Conundrum/ARHGAP18 may have arisen from the tendency to view it in strictly binary terms as upstream or downstream. Here, we propose a third possibility that ARHGAP18 functions as both, participating in a negative feedback loop.

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*We have edited and added data testing if the effects are Rho independent and discussion text in response to the reviewer's comments and clarify the molecular function of ARHGAP18.

"Additionally, focal adhesions and basal actin bundles are restored to WT levels when the ARHGAP18(R365A) GAP-ablated mutant is expressed in ARHGAP18 KO cells (Fig. 5A, B). These results represent the strongest argument that ARHGAP18 functions in additional pathways to RhoA/C alone. Our data suggests that at least one of the alternative pathways is through ARHGAP18's interaction with YAP and Merlin. From these data we conclude that ARHGAP18 has important functions in both RhoA signaling through both its GAP activity and in Hippo signaling through its GAP independent binding partners. "*

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The study is descriptive and contains a series of observations that are not connected. Because of this, the study's conclusions are not well supported, and key mechanistic insight is limited. The study feels like a set of separate observations, that remain incompletely worked out and have some preliminary feel to them. The model in the last figure also seems to contain hypotheses based on the observations, several of which remains to be proven.

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*We present our revised manuscript, in which we've more clearly outlined our rationale and conclusions, as detailed in the above responses, to emphasize the overall connectivity of the study. We have also updated the title of Figure 7 to read "__Theoretical __Model of ARHGAP18's coordination of RhoA and Hippo signaling pathways in Human epithelial cells." To make it clear that we are presenting a working model, which has elements that will require additional investigation. Throughout the manuscript, we highlight the unknown elements that remain to be tested or other outstanding questions. Thus, we do not aim to characterize this complex signaling coordination completely. Instead, this manuscript represents the 3rd iteration in our systematic advances to describe this entirely new signaling pathway. We agree that, despite three separate manuscripts (this one included) to date, this work represents an early stage in understanding the system, many additional studies will be needed to characterize this signaling system fully. Figure 7 is presented as a working model that results from a thoughtful combination of our collective data and that of other researchers, derived from numerous species across decades of study. We firmly believe that proposing such integrative models is valuable for advancing the field. We also recognize the importance of clearly indicating which aspects remain hypothetical. We now explicitly note in several places within the discussion which components of the model will require further validation and experimental confirmation. For example, regarding our theoretical mechanism in Figure 7 we state: *

"Validation of the direct mechanism by which YAP/TAZ transcriptional changes drive basal actin changes in ARHGAP18 KO cells will require further investigation based on predictions from RNAseq results."

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Addressing any possible connection between key effects of ARHGAP18 KO (changes in actin, focal adhesion, integrins, Yap and merlin binding) could strengthen the manuscript. One such specific question is the whether the changes in integrin expression (RNAseq) are indeed connected to the actin alterations and reduction ion focal adhesions (Fig 1). Staining for these integrins to show they are indeed altered, and/or manipulating any of them to reproduce changes could provide and exciting addition.

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*We attempted to stain cells for Integrins by purchasing three separate antibodies. However, despite extensive optimization and careful selection of the specific integrins using our RNAseq results we were unable to get any of these antibodies to work in any cell type or condition. We believe that there is a technical challenge to staining for integrins due to their transmembrane and extracellular components, which we were unable to overcome. As an attempt to address the reviewers comment, we alternatively stained cells for paxillin which directly binds the cytoplasmic tails of integrins (Fig. 3&5). *

Some of the experimental findings are not convincing or lack controls. Fig 1: some of the western blots are not convincing or poor quality. [...] On the same figure, the quality of LIM kinase blots is poor. [...] The signal is weak, and the blot does not appear to support the quantification. The last condition (expression of flag-ARHGAP18) results in a large drop in pLIMK and pcofilin on the blot, which is not reflected by the graph. Addition of *a better blot and the use of strong positive or negative control would boost confidence in these data. *

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In response to this and other reviewers' comments, we have added new western data and quantification to Figure 1. We now focus on MLC/pMLC data as we believe these data highlight the potential Rho-independent mechanism of ARHGAP18, and we were able to greatly improve the quality of the blots through careful optimization. We hope the reviewer finds these blots and quantifications (Fig. 1E and F) more convincing.

*We note that phospho-specific Western blotting presents considerably greater technical challenges than conventional blotting. We believe that the appearance of an attractive looking blot does not always correlate to quality or reproducibility and have focused on taking extraordinarily careful steps in the blotting of our phospho-specific antibodies, which at times comes at the cost of the blot's attractiveness in appearance. For example, all phospho-specific antibodies are run using two color fluorescent markers to blot against both the total protein and the phospho-protein on the same blot. This approach often leads to blots that have reduced signal to noise compared to chemiluminescent Westerns. Additionally, we use phospho-specific blocking buffer reagents which do not contain phosphate-based buffers or agents that attract non-specific phospho-staining signals. These blocking buffers are not as effective as non-fat milk in pbs at blocking the background signal, however, they are ultimately cleaner for phospho-specific primary antibodies. We use carefully optimized protocols, from cell treatment to lysis, transfer, and antibody incubation, including methods developed by laboratories where the corresponding author of the manuscript was trained. Nonetheless, despite these efforts, we have now removed the LIMK and cofilin data because we deemed them unnecessary for the main conclusions of this manuscript and were unable to improve their quality to satisfy the reviewer. *

The changes in pMLC on the western blots are very small, and for any conclusion, these studies require quantification. Further, the expression levels of Flag-ARHGAP18 needs to be shown to support the statement that the protein is expressed, and indeed overexpressed under these conditions (vs just re-expressed).

In continuation of the above comment, we have made significant effort to improve the quality of our pMLC western blots and now provide quantification in Figure 1. We also now provide the Flag-ARHGAP18 signal as requested by the reviewer.

Fig 4: the differences in YAP nuclear localization under the various conditions are not well visible. Quantitation of nuclear/cytosolic signal ratio should be provided. Please provide a rationale and more context for using serum starvation and re-addition. What is the expected effect? Serum removal and addition is referred to as nutrient removal and re-addition, but this is inaccurate, as it does not equal nutrient removal, since serum contains a variety of other important components, e.g. growth factors too.

We have provided new quantification of the nuclear/cytosolic signal ratio in Figure 6D. We have explained our rational for the study through the following new text:

"Merlin is activated and localized to junctions upon signaling, promoting growth and proliferation; among these signals is the availability of growth factors and other components of serum (Bretscher et al., 2002). We hypothesized that since ARHGAP18 formed a complex with Merlin that ARHGAP18's localization may localize to junctions under conditions which promote Merlin activation."

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We have altered our use of "nutrient removal" to "serum removal"

The binding between ARHGAP18 and merlin is interesting, but a key limitation is the use of expressed proteins. Can the binding be shown for the endogenous proteins (IP, colocalization). Another important unaddressed question is the relevance of this binding, and the relation of this to altered YAP nuclear localization.

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*Our data in Fig. 6G shows binding of a resin bound human ARHGAP18 to endogenous YAP from human cells as suggested by the reviewer. In Fig. 6A, we have selected to use GFP-Merlin as Merlin shares approximately 60% sequence identity with Ezrin, Radixin, and Moesin (ERMs). Their similarity is such that Merlin was named for Moesin-Ezrin-Radixin-Like Protein. In our experience, nearly all Merlin or ERM antibodies have some cross-contaminating signal. Thus, a major concern is that if we were to blot for endogenous Merlin in the pull-down experiment, we may see a band that could in fact be ERMs. To avoid this, we tagged Merlin with GFP to ensure that the product pulled down by ARHGAP18 was Merlin, not an ERM. Regarding the ARHGAP18-resin bound column, our homemade ARHGAP18 antibody is polyclonal. We have extensive experience in pulldown assays and have found that the binding of a polyclonal antibody to the bait protein can produce less accurate results, as the binding site for the antibody is unknown and can sterically hinder attachment of target proteins like Merlin. In our experience, attachment to a flag-tag, which is expressed after a flexible linker at the N- or C-terminus, allows us to overcome this limitation, which we've used in this manuscript. *

Minor comments:

Introduction line 99: "When localized to the nucleus, YAP/TAZ promotes the activation of cytoskeletal transcription factors associated with cell proliferation and actin polymerization" Please clarify what you mean by this statement, that is inaccurate in its present for. Did you mean effects on transcription factors that control cytoskeletal proteins, or do you mean that Yap/Taz affect these proteins? Please also provide reference for this.

We've altered the sentence as suggested by the reviewer, which now reads the following:

"When localized to the nucleus, YAP/TAZ promotes transcriptional changes associated with cell proliferation and actin polymerization."

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*The full mechanism for how YAP/TAZ promotes proliferation and actin polymerization is a currently debated issue. We do not think introducing the various current proposed models is required for this manuscript, and we simply intend to convey that when in the nucleus, YAP/TAZ promotes transcriptional changes that drive actin polymerization and cell proliferation. *

-What is the cell confluence in these experiments? For epithelial cells confluence affects actin structure. Please comment on similarity of confluency across experimental conditions?

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All cellular experiments are paired where WT and ARHGAP18 KO cells are plated at the same time under identical conditions. For imaging, we plate all cells onto glass coverslips in a 6 well dish so that each condition is literally in the same cell culture plate and gets identical treatment. In our prior Elife paper studying ARHGAP18, we characterized that ARHGAP18 KO cells and WT cells divide at a similar rate and have similar proliferation characteristics. The epithelial cell cultures are maintained for experiments around 70-80% confluency. For the focal adhesion staining experiments, the confluency is slightly lower, between 50-60% to capture the focal adhesions towards the leading edge. We have added the following new text to further describe these methods: "Cell cultures for experiments were maintained at 70%-80% confluency. For focal adhesion experiments, the cell cultures were maintained at 50%-60% confluency."

-Fig 2 legend: please indicate that the protein detected was non-muscle myosin heavy chain (distinct from the light chain detected in Fig 1).

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We have altered original Figure 2 (new Figure 3) legend.

-Line 339-340: please check the syntax of this sentence -Western blot quantification: the comparison of experiments with samples run on different gels/blots requires careful normalization and experimental consistency. Please describe how this was achieved.

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We have added the following new text to further describe these methods:

"For blots which required quantification of antibodies that were only rabbit primaries (e.g., pMLC/MLC antibodies listed above), samples were loaded onto a single gel and transferred onto a single membrane at the same time. After transfer, the membrane was cut in half and subsequent steps were done in parallel. All quantified blots were checked for equal loading using either anti-tubulin as a housekeeping protein or total protein as detected by Coomassie staining"

Reviewer #3 (Significance (Required)):

Rho signalling is a central regulator of an array of normal and pathological cell functions, and our understanding of the context dependent regulation of this key pathway remains very incomplete. Therefore, new knowledge on the role of specific regulators, such as ARHGAP18, is of interest to a very broad range of researchers. A further exciting aspect of this protein, that despite indications by many studies that it acts as a GAP (inhibitor) for Rho proteins, there are findings in the literature that suggest that its manipulation can affect actin in unexpected (opposite) manner. These point to possible Rho-independent roles, and warranted further in-depth exploration.

One of the strength of the study is that it explores possible roles of ARHGAP18 beyond RhoA and describes some new and interesting observations, which advance our knowledge. The authors use some excellent tools (e.g. ARHGAP KO cells and re-expression) and approaches (e.g. super resolution microscopy to analyze actin changes, RNAseq and bioinformatics to find genes that may be downstream from ARHGAP18). A key limitation of the study however, is that it is not clear whether the observed findings are indeed independent from RhoA. Further limitation is that potential causal relationships between the described findings are not studied, and therefore the findings are in some cases overinterpreted, and limited mechanistic insights are provided. In some cases the exclusive use of expressed proteins is also a limitation. Finally, some of the experiments also need improvement.

Reviewer expertise: RhoA signalling, guanine nucleotide exchange factors, epithelial biology, cell migration, intercellular junctions.

In the above comments, we detail the new experimental data addressing reviewer 3's listed key limitations. We've added new data using the Rho GAP deficient ARHGAP18(R365A) variant which allows for the direct characterization of ARHGAP18's Rho independent activity. We have introduced new data in WT cells studying endogenous proteins to address the limitations from expressed proteins. Finally, we have moderated our language to address overinterpretation. Collectively, we believe that our revised manuscript addresses the constructive reviewer's comments.

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

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Reply to the reviewers

Dear editor and reviewers,

We sincerely thank you for your thoughtful comments and constructive suggestions, which have greatly improved the quality and clarity of our manuscript. In response, we have implemented all requested changes, which are highlighted in yellow throughout the revised text, and updated several figures accordingly. Furthermore, we have performed all additional experiments recommended by the reviewers and incorporated the new data into the manuscript. To enhance clarity, we have also included a schematic representation of our proposed model in an additional figure, providing a concise visual summary of our findings.

We hope that these revisions fully address all concerns raised by the reviewers and meet all the expectations for publication.

Below, we answer the reviewers point by point (in blue).

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

In this paper, the authors address the important question of the role of centrosomes during neuronal development. They use Drosophila as an in vivo model. The field is somewhat unclear on the role and importance of centrosomes during neuronal development, although the current data would suggest they are dispensable for axon specification and growth. Early studies in cultured mammalian neurons showed that centrosomes are active and that their microtubules can be cut and transported into the neurites. But a study then showed that centrosomes in these cultured neurons are deactivated relatively early during neuronal development in vitro and that ablating centrosomes even when they are active had no obvious effect on axon specification and growth. Consistent with this, a study in Drosophila provided evidence that centrosomes were not active or necessary in different types of neurons. More recently, a study showed that centrosomal microtubules are dispensable for axon specification and growth in mice in vivo but are required for neuronal migration in the cerebral cortex. However, another study has linked the generation of acetylated microtubules at centrosomes with axon development. In this current study, the authors examine the effect of centrosome loss on various motor and sensory neurons and muscles mainly by examining mutants in essential centriole duplication genes. They associate axonal routing and morphology defects with centrosome loss and provide some evidence that centrosomes could still be active in the developing neurons. Overall, they conclude that centrosomes are active during at least early neuronal development and that this activity is important for proper axonal morphology and routing.

While I think this study addressing a very interesting and important question, I think as it stands the data is not sufficient to be conclusive on a role for centrosomes during neuronal development. My biggest concern is that most phenotypes have not yet been shown to be cell autonomous, as whole animal mutants have been analysed rather than analysing the effect of cell-specific depletion, and the evidence for active centrosomes needs to be strengthened. If the authors can provide stronger evidence for a role of centrosomes in axonal development then the paper will certainly be of interest to a broad readership.

We thank the reviewer for the clear and concise summary and fully agree that our study addresses a critical gap in understanding. Centrosomes have long been implicated in morphogenesis, yet their precise contribution to nervous system development has remained unclear. Our findings provide compelling evidence that centrosomes are indispensable for proper nervous system formation and that their absence also triggers muscular defects, highlighting their broader role in tissue organization.

We acknowledge that the original manuscript lacked some key details; therefore, we have now strengthened our conclusions with additional experiments. Specifically, we demonstrate that these effects are cell-autonomous by using two independent RNAi lines targeted to a subset of motor neurons. Furthermore, we present new data showing that neuronal centrosomes remain active during the early stages of axonal development, emphasising their functional relevance in morphogenesis. All new experiments, figures, and corresponding text revisions are detailed below.

Major comments 1) The sas-6 transallelic combination shows only 17% embryonic lethality compared to 50% embryonic lethality with sas-4 mutants. Given that both mutants should result in the same degree of centrosome loss (this should be quantified in sas-6 mutants) it would suggest that either sas-4 has other roles away from centrosomes or that the sas-4 mutant chromosome used in the experiment has other mutations that affect viability. The effect of picking up "second-site lethal" mutations on mutant chromosomes is common and so I would not be surprised if this is the reason for the difference in phenotypes. This can be addressed either by "cleaning up" the sas-4 mutant chromosome by backcrossing to wild-type lines, allowing recombination to occur and replace the potential second site mutations, or by using transallelic combinations of sas-4, as they did for sas-6. The "easier" option may just be to analyse all the phenotypes with the sas-6 transallelic combination.

We appreciate this comment, as it brought to light an issue with the CRISPR line Sas-6-Δa. Upon reanalysing all the data, we determined that this line is embryonic lethal both in homozygosis and when combined with the deficiency uncovering the genomic region, Df(3R)BSC794. In contrast, Sas-6-Δb homozygotes are viable. The inconsistency between these results raised concerns about whether the Δa and Δb Sas-6 mutants carry deletions confined to the Sas-6 coding region. Although this would not hinder our cell biology analysis, it could represent a problem in viability tests. To address this, we repeated all analyses using Sas-6-Δb homozygotes and Sas-6-Δb combined with Df(3R)BSC794. These new results are more consistent and indicate that approximately 50% of Sas-6/Def individuals hatch as adults. Fig. 3 was redone and the manuscript text changed in view of these results.

2) Using "whole animal" mutants for assessing neuronal morphology is risky due to non-cell-autonomous effects. The authors have carried out some phenotypic analysis of neurons depleted of Sas-4 by cell-specific RNAi, but I feel they need to do this for all of their analysis. This includes embryonic lethality measures, quantification of centrosome numbers, and all axonal phenotypes in Sas-4 RNAi neurons. It would also be prudent to use 2 distinct RNAi lines to help ensure any phenotypes are not off-target effects (and this may help clarify why the authors see some additional phenotypes with RNAi). Indeed, there are relatively weak phenotypes in muscles when using RNAi compared to the mutants and these potential non-cell-autonomous effects could then have a knock-on effect on neuronal morphology. If the authors were concerned that RNAi is not very efficient (explaining any potential weaker phenotypes than in mutants) the authors could examine the effectiveness of RNAi lines by analysing protein depletion by western blotting or mRNA depletion by rt-qPCR (although this has to be done in a different cell type due to the difficulty in obtaining a neuronal extract).

We have now added a new panel to supplementary Figure 1, showing how the expression of a different Sas-4 RNAi line (2) induces similar nervous system phenotypes when expressed only in aCC, pCC and RP2 pioneer neurons (Sup. Fig. 1 M-O).

3) When analysing centriole presence or absence it is a good idea to stain with two different centriole markers e.g. Asl and Plp. This helps rule out unspecific staining. It is clear from the images that similar sized foci can be observed outside of the cells (see Figure 5A for example), so clearly some of the foci that appear to be within the cells may also be unspecific staining.

In a new supplementary figure, we now show that Asl and Plp colocalize and quantify the number of times we find this colocalization in neurons (Supl. Fig 3). In addition, and we apologise for the confusion, but the reason why there are foci outside the marked cells is because these are wholemount embryonic stainings and the anti-Plp antibody marks all centrosomes in all cells in the embryo.

4) The evidence for active centrosomes is not that convincing. Acetylated tubulin is associated with stable MTs, which are not normally organised by "active" centrosomes that nucleate dynamic microtubules. Moreover, it is plausible that centriole foci happen to overlap with the acetylated tubulin staining by chance. This would explain why not all centrosomes colocalise with acetylated tubulin signal. The authors could better test centrosome activity by performing live imaging with EB1-GFP. If centrosomes are active, it is very easy to observe the many comets produced by the centrosomes.

We appreciate the reviewer’s comment and agree that acetylated tubulin alone is not an ideal marker for centrosome activity. To address this, we performed live imaging of aCC neurons expressing EB1-GFP together with Asl-Tomato. This was technically challenging because we were imaging only two neurons per segment in live embryos, under significant limitations in fluorescence detection and timing. Despite these constraints, we were able to clearly observe EB1 comets emerging from the centrosome and moving toward the cell periphery, providing direct evidence of microtubule nucleation from centrosomes in neurons.

Importantly, we complemented this with a microtubule depolymerization/polymerization assay, which provides unequivocal evidence that polymerization initiates at the centrosome. After depolymerization, we observed microtubule regrowth from the centrosome, confirming its role as an active microtubule-organizing centre in these neurons. Together, we hope that these results are enough to demonstrate that neuronal centrosomes are functionally active during early axonal development. These experiments are presented in Figure 6 and corresponding text in the manuscript.

5) If the authors believe that centrosomes have a role in axon pathfinding in sensory neurons, they should show that these centrosomes are active, at least during early stages (again using EB1-GFP imaging).

We appreciate the reviewer’s suggestion and agree that EB1-GFP imaging would be the most direct way to assess centrosome activity in sensory neurons. However, performing time-lapse imaging in these neurons is technically very demanding due to their location and accessibility in live embryos, and we did not attempt this approach. Instead, we now provide new evidence showing that sensory neuron centrosomes colocalize with both α-tubulin and γ-tubulin. This strongly supports that these centrosomes are associated with microtubule nucleation machinery and are as likely as motor neuron centrosomes to be active during early stages of axon development. These new data have been included in the revised manuscript (see Figure 5 and corresponding text).

6) The authors mention in the discussion that "increased JNK activity, can result in axonal wiggliness (Karkali et al, 2023)". I therefore wonder whether centrosome loss may induce JNK activation (the stress response), as this would then indicate an indirect effect of centrosome loss on axonal structure rather than a direct influence of centrosome-generated microtubules. The authors could assess whether the DNK-JNK pathway is activated in neurons lacking centrosomes by expression UAS-Puc-GFP and quantifying the nuclear signal.

In a new supplementary figure, we now show by using a reporter for JNK signalling, as requested, that Sas-4 neurons do not activate the JNK pathway (Supl. Fig 4).

7) In Figure 5, the authors claim that they find "a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". I don't think this is a strong correlation. The difference in centriole number between embryos with no defects and those with defects is very small. In contrast, the difference between centriole numbers in control (no defects) and mutant (no defects) is very large. So, there does not appear to be a strong correlation between centrosome number and phenotype.

We agree and we have corrected this sentence to better explain the results.

Minor comments

1) I don't understand Figure 3C - why do the % of surviving homozygotes and heterozygotes add up to 100%? Should the grey boxes not relate to dead and the white to surviving?

Thank you for pointing this out. Figures 1B and 3C represent only the surviving individuals. The grey boxes correspond to surviving homozygotes, and the white boxes correspond to surviving heterozygotes. The percentages add up to 100% only at embryonic stages because all embryos reach late embryonic stages. The grey and white boxes reflect the proportion of these two genotypes among the survivors, not the total number of embryos including those that died. We have changed the text to convey this.

2) "In mouse fibroblasts, myoblasts and endothelial cells, centrosome orientation is important for nuclear positioning and cell migration(Chang et al, 2015; Gomes et al, 2005; Kushner et al, 2014)." Do you mean "centrosome position"?

Yes, text changed, thank you for spotting it.

3) In the introduction, the authors mention Meka et al. when saying the centrosomal microtubules are important for axonal development, but they should also discuss the counter argument from Vinopal et al., 2023 (Neuron) that showed how centrosomes were required for neuronal migration but not axon growth, which was instead mediated by Golgi-derived microtubules.

Done, thank you very much.

4) Lines 228-230 - repeated sentence

Corrected, thank you very much.

5) Additionally, we did not detect centrioles in the quadrant opposite the axon exit point (Fig. 2B n=75) - this data is not in Fig 2B

Correct, it is in figure 4B, thank you very much.

6) "This significant decrease in the humber of centrioles further supports the critical role of Sas-4 in pioneer neurons of the ventral nerve cord (VNC) during Drosophila embryogenesis". It rather highlights that Sas-4 is required for centriole formation in these neurons. Also, humber = number.

We agree, and have changed the text, thank you very much.

7) Result title: Non-ciliated sensory neurons have centrioles. This is kind of obvious. A better title may be "axon phenotypes correlate with centriole numbers in sensory neurons" but unfortunately i don't think there is good evidence for this (See major point above).

We agree and we have changed. We now believe we have strong evidence to support it. We hope the additional data presented in the revision convincingly demonstrate this point.

Reviewer #1 (Significance (Required)):

As mentioned above, the advance will be important if more evidence is provided. In this case, the paper will be interesting to a broad readership. But currently the paper is limited by the lack of evidence for centrosome function and activity in the neurons.

We hope that reviewer 1, now considers that the manuscript is not limited anymore and that it shows convincing evidence for centrosome function and activity in embryonic neurons.

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

Summary: In this manuscript, Gonzalez et al. examine the potential function of centrosomes in the neurons and muscle cells of Drosophila embryos. By studying various mutant and RNAi lines in which centriole duplication has been disrupted, they conclude that the loss of centrioles disrupts axonal pathfinding and muscle integrity.

Major points: 1. Throughout the manuscript, the phenotypes presented are often quite subtle. For this reason, I would really recommend that these experiments are scored blind. Perhaps the authors did this, but I didn't see any mention of this.

All our phenotypic analyses are performed blind. We apologize for not having originally included this information in the Methods section; it has now been added. Embryos are stained using colorimetric methods (DAB) to label the nervous system, while balancer chromosomes are marked with a fluorescent antibody. This approach allows us to assess and quantify phenotypes using white light without knowing whether the embryos are homozygous mutants or heterozygous, which can only be detected by changing the channels to fluorescence.

1. The authors conclude that neurons have active centrioles that function as centrosomes (Figure 6), but the data here is confusing. The authors state that in these cells they observe acetylated MTs extending from the centrosomes and these colocalised with g-tubulin. But the authors don't show the overlap between centrosomes, g-tubulin and MTs, as they stain for these separately. This is problematic, as it was not clear from these images that the majority of the MTs really are extending from the centrosome: the centrosome may just associate or be close by to these MT cables (Figure 6A,B). Moreover, the authors show that only a fraction of the centrosomes in these cells associate with g-tubulin, so presumably in cells where the centrosomes lack g-tubulin they would not expect the centrosomes to be associated with the MTs-but they do not show that this is the case. Perhaps the authors can't test this, but an alternative would be to show that these MT arrays are absent in Sas-4 mutants. This would give more confidence that these MTs arise from the centrosomes.

We agree that the initial data based on acetylated microtubules and γ-tubulin colocalization were not sufficient to conclude that microtubules originate from the centrosome, as these markers can only suggest association. To address this, we have now included additional experiments that provide direct evidence of centrosome activity.

First, we performed live imaging of aCC neurons expressing EB1-GFP together with Asl-Tomato. Despite the technical challenges of imaging only two neurons per segment in live embryos under strict fluorescence and timing constraints, we were able to clearly observe EB1 comets emerging from the centrosome and moving toward the cell periphery. This demonstrates active microtubule nucleation from centrosomes rather than mere proximity to microtubule bundles.

Second, we carried out a microtubule depolymerization/polymerization assay, which provides unequivocal evidence that polymerization initiates at the centrosome. After depolymerization, microtubules regrew from the centrosome, confirming its role as an active microtubule-organizing center. These experiments go beyond colocalization and directly address the concern that centrosomes might simply be adjacent to microtubule cables.

Regarding the suggestion to use Sas-4 mutants, while we did not perform this experiment, the regrowth assay combined with EB1 imaging strongly supports that these microtubules originate from the centrosome. All new data are presented in Figure 6 and the corresponding text in the revised manuscript.

1. The authors show that muscle cell integrity is compromised by centriole-loss (Figure 2). This is very surprising as it is widely believed that centrosomes are non-functional in muscle cells, and the MTs are instead organised around the nuclear envelope. I'm not aware of the situation in Drosophila muscle cells, but the authors should ideally try to examine if the centrioles are functioning as centrosomes in these cells. At the very least they should discuss how they think centriole-loss is influencing the muscle integrity when it is widely believed they are inactive in these cells.

We do not claim that centrosomes are active in muscle cells at these developmental stages. The observed muscle defects could result from earlier processes such as cell division, migration, or muscle fusion. We agree that this is an intriguing observation; however, pursuing this question further would go beyond the scope of the current manuscript. As requested by the reviewer, we have now expanded the discussion to consider how centriole loss might impact muscle integrity.

Regardless of the strength of the supporting data, I think the authors should tone down their conclusions. The title and abstract led me to believe that centriole loss would cause significant problems in axonal pathfinding and muscle integrity. In all the mutant specimens examined (and certainly the low magnification views shown in Figure 1D'-F', Figure 1I'-K' and Figure 2D'-F') the mutants look very similar to the WT. Many readers may not get past the title and abstract, so the authors should make it clearer that these defects are very subtle.

We have changed the text to convey this idea.

Minor points: 1. In Figures 4 and 5, CP309 staining is relied on to identify centrioles, but there is quite a background of non-specific dots, making it hard to be certain what is a centriole and what isn't. For example, in Figure 5D' there are lots of dots within some of the cells - are any of these centrioles? How can the authors be certain which dot is a centriole in some of the cells shown in Figure 5C'? Is it possible to use a second marker and only count as centrioles dots that are recognised by both antibodies?

We thank the reviewer for this suggestion and agree that using a second marker improves confidence in centriole identification. In a new supplementary figure (Supplementary Fig. 3), we now show that Asl and Plp colocalize in neurons and provide a quantification of the frequency of this colocalization. This dual labelling confirms the identity of centrioles and addresses the concern about non-specific background.

We also apologize for any confusion regarding the presence of foci outside the marked cells. These images are whole-mount embryonic stainings, and the anti-Plp antibody labels all centrosomes in all cells of the embryo, which explains the additional foci observed.

In the abstract that authors state that traditionally centrosomes have been considered to be non-essential in terminally differentiated cells. I don't think this is correct. In the standard "textbook" view of a cell, the centrosome is normally positioned in the centre of the cell organising an extensive array of MTs that are thought play an important role in organising intracellular transport, the positioning and movement of organelles and the maintenance and establishment of cell polarity. I don't think it is only recent evidence that suggests they play vital roles in terminally differentiated cells.

We thank the reviewer for this correction and we have changed the text accordingly.

1. Line 162 the authors state that in the RNAi knockdown lines they observe several additional phenotypes, but then in the same sentence (Line 164) they say that these defects were also observed in the original mutant and mutant/Df lines.

We apologise for this confusion, we have rearranged the sentence for clearance.

The sentences in Line281-287 don't reference any of the Figures, so it seems the authors are just stating these results without presenting any data (e.g. "Significantly, we also found a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". If they've tested this correlation, they should show it.

We have rearranged the sentences for better understanding.

In Figure 7 I did not understand how the authors measured tortuosity (wiggliness) and could see no description in the methods. This is important as, again the defect seems quite subtle, but perhaps I am not understanding which bits of the axon are being measures. Is it just the small bit of the axons close to the asterixis that is being measured, or the whole FasII track?

We have now added another quantification and additional descriptions in the methods section.

Reviewer #2 (Significance (Required)):

The potential function of centrosomes in axonal outgrowth is quite controversial, so this study is potentially of considerable interest.

However, several aspects of the data presented here were confusing or not terribly convincing. In its present state, I don't think the main conclusions are strongly enough supported by the data.

We hope that reviewer 2, now considers that the manuscript is not confusing anymore and that it shows convincing evidence for centrosome function and activity in embryonic neurons.

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

The manuscript of González et al. entitled "Centriole Loss in Embryonic Development Disrupts Axonal Pathfinding and Muscle Integrity" deals with the role of centrosomes in shaping axonal morphology. To this aim the AA analysed Drosophila Sas-4 mutants that are reported to develop until adult stage without centrioles. Remarkably, the AA observe that 50% of the homozygous mutant embryos fail to hatch as larvae. The present observations suggest that centrosome loss results in axonemal shaping defects and muscle developmental abnormalities. Finally, the AA show the presence of functional centrosomes in neurons. In my opinion, the manuscript is interesting because shows unexpected findings. However, to justify these new findings the AA are required to improve some experimental observations.

We thank the reviewer for his summary of our work and for considering it interesting. We have taken into account all the comments and believe that these have helped improve our manuscript.

Major: Abstract- It is unclear in which phenotypic condition the observations of centrosome loss or centrosome presence have been found. Please better explain. l.36. embryos, larvae, adult, from Sas4 or controls? If mutants, the observations are very interesting since Sas4 would be without centrioles. Indeed, Basto et al., show that chemosensory neurons do not develop an axoneme in the absence of centrioles, but extend dendrites toward the sensory bristle.

We have made clear which refer to wild-type and which are Centriole Loss (CL) conditions. CL conditions refer to mutant and downregulation conditions, whereas targeted downregulation refers to RNAi downregulation only in neurons.

I do not think appropriate the use of "centriole" in the main title since the centrioles would be localized by true centriolar antigens rather than by centrosomal antigens. This problem occurs throughout the text and some figures where the AA image centrioles by centrosomal material. In Gig. 5A only the AA properly look at Asl localization. The other pictures of presumptive centrioles or centriole quantification report CP309 dots. This localization does not unequivocally reveal centrioles, since CP309 is essentially required for centrosome-mediated Mt nucleation. There are differentiated Drosophila tissues in which centrioles are present, but inactivated, and unable to recruit pericentriolar material. Mt are nucleated by ncMTOCs that contain centrosomal material and gamma-tubulin. Thus, the centrosomal antigens do not colocalize with centrioles.

We have changed centrioles to centrosomes in the title and most sections in the manuscript. We have also included an extra control, showing that Asl and Plp colocalize and quantify the number of times we find this colocalization in neurons (Supl. Fig 3). Asl is a reliable and widely used marker for centrioles, as it localizes specifically to the centriole structure (Varmark H, Llamazares S, Rebollo E, Lange B, Reina J, Schwarz H, Gonzalez C. Asterless is a centriolar protein required for centrosome function and embryo development in Drosophila. Curr Biol. 2007 Oct 23;17(20):1735-45. doi: 10.1016/j.cub.2007.09.031. PMID: 17935995.)

Minor: l. 58. The early arrest is mainly due to a checkpoint control. In double mutant for Sas4 and P53 the embryos survive longer, even if their further development is asrrested.

We thank the reviewer for this comment, and we have changed the text accordingly.

1. Previous works, also quoted by the AA, reported that in mature neurons the centrosome are inactivated, whereas the present manuscript describes functional centrosomes in Drosophila motor and peripheral nervous system. This is an intriguing observations that needs a better explanation in Discussion section.

We thank the reviewer for this comment, and we have changed the discussion accordingly.

l.143-145. I understand that 50% of the Sas4 embryos that reach the adult stage have centrioles. Is it correct? But if it is so, how the AA explain the absence of centrioles in sensory neurons of adult flies as reported by Basto et al. ?

According to our results they have less centrioles than controls already at embryonic stages. In addition, as reported in Basto et al. they continue losing centrioles during larval stages and metamorphosis, which explains why centrioles are not detected at adult stages.

l.215. It is unclear for me why the AA analyse Sas6 flies, unless explain the mutant phenotype.

To strengthen our conclusions with Sas-4 and exclude the possibility that the observed phenotypes arise from a centrosome-independent function of Sas-4. For this reason, we have taken additional steps to confirm that the effects are specifically due to centrosome loss and we used Sas-6 mutants as one of these.

l.221. How the centrioles have been quantified? What antibody, the AA used.

We have quantified centrosomes using antibodies agains Plp (CP309) and Asl-YFP expression.

l.244. and Fig 4C,D. I see high background with CP309. As reported previously I think better to use antibodies against centriolar proteins, such as Sas6, Ana1, Asl, or Sas4 ( if centrioles are present in 50% of mutants as the AA claim, the antibody could be also useful). In addition, I can see some CP309 spots in Fig 4E,F. Are they centrioles?

Indeed, as we report, Sas-4 mutant embryos are not totally devoid of centrosomes. In addition, and we apologise for the confusion, but the reason why there are foci outside the marked cells in control embryos is because these are wholemount embryonic stainings and the anti-Plp antibody marks all centrosomes in all cells in the embryo, not just in the neurons.

l.270 and Fig. 5A and Fig.5 C-E. Why the AA localize Cp309 and not Asl (Fig. 5A) to detect centrioles?

In a new supplementary figure, we now show that Asl and Plp colocalize and quantify the number of times we find this colocalization in neurons (Supl. Fig 3). So, we can use CP309 in neurons to the same effect as Asl-

L295-296. I cannot see Mts, but only a diffuse staining. I am expecting to see distinct Mt bundles.

In figure 5 it is now easier to see the MT bundles in the new experiment in Fig. 5F-I , where we performed MT depolymerisation/repolymerisation: Nevertheless, we need to stress out that we are doing these analyses in wholemount embryonic stainings.

326-327. How the AA explain this different lethality, even if both the proteins are involved in centriole assembly?

We have now redone all the viability and mutant phenotype analysis using Sas-6 CRISPR mutant over the Deficiency, which is a better way to access the phenotype.

335-337. In my opinion the quoted publications are not relevant.

We believe that these references back up our hypothesis because:

• Metzger et al 2012 stress the importance of nuclear position in muscle development in Drosophila
• Loh et al 2023, relate centrosomes with nuclear migration in Drosophila
• Tillery et al 2018, is a review describing MTs in muscle development in Drosophila.

358-359. Does maternal contribution persist after gastrulation?

While bulk degradation occurs by midblastula transition, some stable maternal products persist beyond gastrulation. In our case, if centrioles are formed due to the maternal contribution, they will only be diluted by cell division, which explains why we can detect centrioles at late embryonic stages.

l.366. This is an intriguing point, but as previously observed I have some problem with centriole localization. References. Please uniform Journal abbreviations and control page numbers.

I hope we have clarified this problem with the new experiments showing MT repolarization from the centrosomes in neurons.

Reviewer #3 (Significance (Required)):

The manuscript is potentially interesting for peoples working of cell and molecular biology, and development. However, the paper needs an additional working to be suitable for publication.

We hope that reviewer 3, considers that the additional work and revision make this manuscript suitable for publication.

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Referee #2

Evidence, reproducibility and clarity

Summary: In this manuscript, Gonzalez et al. examine the potential function of centrosomes in the neurons and muscle cells of Drosophila embryos. By studying various mutant and RNAi lines in which centriole duplication has been disrupted, they conclude that the loss of centrioles disrupts axonal pathfinding and muscle integrity.

Major points:

1. Throughout the manuscript, the phenotypes presented are often quite subtle. For this reason, I would really recommend that these experiments are scored blind. Perhaps the authors did this, but I didn't see any mention of this.
2. The authors conclude that neurons have active centrioles that function as centrosomes (Figure 6), but the data here is confusing. The authors state that in these cells they observe acetylated MTs extending from the centrosomes and these colocalised with g-tubulin. But the authors don't show the overlap between centrosomes, g-tubulin and MTs, as they stain for these separately. This is problematic, as it was not clear from these images that the majority of the MTs really are extending from the centrosome: the centrosome may just associate or be close by to these MT cables (Figure 6A,B). Moreover, the authors show that only a fraction of the centrosomes in these cells associate with g-tubulin, so presumably in cells where the centrosomes lack g-tubulin they would not expect the centrosomes to be associated with the MTs-but they do not show that this is the case. Perhaps the authors can't test this, but an alternative would be to show that these MT arrays are absent in Sas-4 mutants. This would give more confidence that these MTs arise from the centrosomes.
3. The authors show that muscle cell integrity is compromised by centriole-loss (Figure 2). This is very surprising as it is widely believed that centrosomes are non-functional in muscle cells, and the MTs are instead organised around the nuclear envelope. I'm not aware of the situation in Drosophila muscle cells, but the authors should ideally try to examine if the centrioles are functioning as centrosomes in these cells. At the very least they should discuss how they think centriole-loss is influencing the muscle integrity when it is widely believed they are inactive in these cells.
4. Regardless of the strength of the supporting data, I think the authors should tone down their conclusions. The title and abstract led me to believe that centriole loss would cause significant problems in axonal pathfinding and muscle integrity. In all the mutant specimens examined (and certainly the low magnification views shown in Figure 1D'-F', Figure 1I'-K' and Figure 2D'-F') the mutants look very similar to the WT. Many readers may not get past the title and abstract, so the authors should make it clearer that these defects are very subtle.

Minor points:

1. In Figures 4 and 5, CP309 staining is relied on to identify centrioles, but there is quite a background of non-specific dots, making it hard to be certain what is a centriole and what isn't. For example, in Figure 5D' there are lots of dots within some of the cells - are any of these centrioles? How can the authors be certain which dot is a centriole in some of the cells shown in Figure 5C'? Is it possible to use a second marker and only count as centrioles dots that are recognised by both antibodies?
2. In the abstract that authors state that traditionally centrosomes have been considered to be non-essential in terminally differentiated cells. I don't think this is correct. In the standard "textbook" view of a cell, the centrosome is normally positioned in the centre of the cell organising an extensive array of MTs that are thought play an important role in organising intracellular transport, the positioning and movement of organelles and the maintenance and establishment of cell polarity. I don't think it is only recent evidence that suggests they play vital roles in terminally differentiated cells.
3. Line 162 the authors state that in the RNAi knockdown lines they observe several additional phenotypes, but then in the same sentence (Line 164) they say that these defects were also observed in the original mutant and mutant/Df lines.
4. The sentences in Line281-287 don't reference any of the Figures, so it seems the authors are just stating these results without presenting any data (e.g. "Significantly, we also found a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". If they've tested this correlation, they should show it.
5. In Figure 7 I did not understand how the authors measured tortuosity (wiggliness) and could see no description in the methods. This is important as, again the defect seems quite subtle, but perhaps I am not understanding which bits of the axon are being measures. Is it just the small bit of the axons close to the asterixis that is being measured, or the whole FasII track?

Significance

The potential function of centrosomes in axonal outgrowth is quite controversial, so this study is potentially of considerable interest.

However, several aspects of the data presented here were confusing or not terribly convincing. In its present state, I don't think the main conclusions are strongly enough supported by the data.

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

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

In this paper, the authors address the important question of the role of centrosomes during neuronal development. They use Drosophila as an in vivo model. The field is somewhat unclear on the role and importance of centrosomes during neuronal development, although the current data would suggest they are dispensable for axon specification and growth. Early studies in cultured mammalian neurons showed that centrosomes are active and that their microtubules can be cut and transported into the neurites. But a study then showed that centrosomes in these cultured neurons are deactivated relatively early during neuronal development in vitro and that ablating centrosomes even when they are active had no obvious effect on axon specification and growth. Consistent with this, a study in Drosophila provided evidence that centrosomes were not active or necessary in different types of neurons. More recently, a study showed that centrosomal microtubules are dispensable for axon specification and growth in mice in vivo but are required for neuronal migration in the cerebral cortex. However, another study has linked the generation of acetylated microtubules at centrosomes with axon development. In this current study, the authors examine the effect of centrosome loss on various motor and sensory neurons and muscles mainly by examining mutants in essential centriole duplication genes. They associate axonal routing and morphology defects with centrosome loss and provide some evidence that centrosomes could still be active in the developing neurons. Overall, they conclude that centrosomes are active during at least early neuronal development and that this activity is important for proper axonal morphology and routing.

While I think this study addressing a very interesting and important question, I think as it stands the data is not sufficient to be conclusive on a role for centrosomes during neuronal development. My biggest concern is that most phenotypes have not yet been shown to be cell autonomous, as whole animal mutants have been analysed rather than analysing the effect of cell-specific depletion, and the evidence for active centrosomes needs to be strengthened. If the authors can provide stronger evidence for a role of centrosomes in axonal development then the paper will certainly be of interest to a broad readership.

Major comments

1. The sas-6 transallelic combination shows only 17% embryonic lethality compared to 50% embryonic lethality with sas-4 mutants. Given that both mutants should result in the same degree of centrosome loss (this should be quantified in sas-6 mutants) it would suggest that either sas-4 has other roles away from centrosomes or that the sas-4 mutant chromosome used in the experiment has other mutations that affect viability. The effect of picking up "second-site lethal" mutations on mutant chromosomes is common and so I would not be surprised if this is the reason for the difference in phenotypes. This can be addressed either by "cleaning up" the sas-4 mutant chromosome by backcrossing to wild-type lines, allowing recombination to occur and replace the potential second site mutations, or by using transallelic combinations of sas-4, as they did for sas-6. The "easier" option may just be to analyse all the phenotypes with the sas-6 transallelic combination.
2. Using "whole animal" mutants for assessing neuronal morphology is risky due to non-cell-autonomous effects. The authors have carried out some phenotypic analysis of neurons depleted of Sas-4 by cell-specific RNAi, but I feel they need to do this for all of their analysis. This includes embryonic lethality measures, quantification of centrosome numbers, and all axonal phenotypes in Sas-4 RNAi neurons. It would also be prudent to use 2 distinct RNAi lines to help ensure any phenotypes are not off-target effects (and this may help clarify why the authors see some additional phenotypes with RNAi). Indeed, there are relatively weak phenotypes in muscles when using RNAi compared to the mutants and these potential non-cell-autonomous effects could then have a knock-on effect on neuronal morphology. If the authors were concerned that RNAi is not very efficient (explaining any potential weaker phenotypes than in mutants) the authors could examine the effectiveness of RNAi lines by analysing protein depletion by western blotting or mRNA depletion by rt-qPCR (although this has to be done in a different cell type due to the difficulty in obtaining a neuronal extract).
3. When analysing centriole presence or absence it is a good idea to stain with two different centriole markers e.g. Asl and Plp. This helps rule out unspecific staining. It is clear from the images that similar sized foci can be observed outside of the cells (see Figure 5A for example), so clearly some of the foci that appear to be within the cells may also be unspecific staining.
4. The evidence for active centrosomes is not that convincing. Acetylated tubulin is associated with stable MTs, which are not normally organised by "active" centrosomes that nucleate dynamic microtubules. Moreover, it is plausible that centriole foci happen to overlap with the acetylated tubulin staining by chance. This would explain why not all centrosomes colocalise with acetylated tubulin signal. The authors could better test centrosome activity by performing live imaging with EB1-GFP. If centrosomes are active, it is very easy to observe the many comets produced by the centrosomes.
5. If the authors believe that centrosomes have a role in axon pathfinding in sensory neurons, they should show that these centrosomes are active, at least during early stages (again using EB1-GFP imaging).
6. The authors mention in the discussion that "increased JNK activity, can result in axonal wiggliness (Karkali et al, 2023)". I therefore wonder whether centrosome loss may induce JNK activation (the stress response), as this would then indicate an indirect effect of centrosome loss on axonal structure rather than a direct influence of centrosome-generated microtubules. The authors could assess whether the DNK-JNK pathway is activated in neurons lacking centrosomes by expression UAS-Puc-GFP and quantifying the nuclear signal.
7. In Figure 5, the authors claim that they find "a correlation between axonal guidance phenotypes and the numbers of centrioles per embryo". I don't think this is a strong correlation. The difference in centriole number between embryos with no defects and those with defects is very small. In contrast, the difference between centriole numbers in control (no defects) and mutant (no defects) is very large. So, there does not appear to be a strong correlation between centrosome number and phenotype.

Minor comments

1. I don't understand Figure 3C - why do the % of surviving homozygotes and heterozygotes add up to 100%? Should the grey boxes not relate to dead and the white to surviving?
2. "In mouse fibroblasts, myoblasts and endothelial cells, centrosome orientation is important for nuclear positioning and cell migration(Chang et al, 2015; Gomes et al, 2005; Kushner et al, 2014)." Do you mean "centrosome position"?
3. In the introduction, the authors mention Meka et al. when saying the centrosomal microtubules are important for axonal development, but they should also discuss the counter argument from Vinopal et al., 2023 (Neuron) that showed how centrosomes were required for neuronal migration but not axon growth, which was instead mediated by Golgi-derived microtubules.
4. Lines 228-230 - repeated sentence
5. Additionally, we did not detect centrioles in the quadrant opposite the axon exit point (Fig. 2B n=75) - this data is not in Fig 2B
6. "This significant decrease in the humber of centrioles further supports the critical role of Sas-4 in pioneer neurons of the ventral nerve cord (VNC) during Drosophila embryogenesis". It rather highlights that Sas-4 is required for centriole formation in these neurons. Also, humber = number.
7. Result title: Non-ciliated sensory neurons have centrioles. This is kind of obvious. A better title may be "axon phenotypes correlate with centriole numbers in sensory neurons" but unfortunately i don't think there is good evidence for this (See major point above).

Significance

As mentioned above, the advance will be important if more evidence is provided. In this case, the paper will be interesting to a broad readership. But currently the paper is limited by the lack of evidence for centrosome function and activity in the neurons.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Reviews):

Summary:

Argunşah et al. describe and investigate the mechanisms underlying the differential response dynamics of barrel vs septa domains of the whisker-related primary somatosensory cortex (S1). Upon repeated stimulation, the authors report that the response ratio between multi- and single-whisker stimulation increases in layer (L) 4 neurons of the septal domain, while remaining constant in barrel L4 neurons. This difference is attributed to the short-term plasticity properties of interneurons, particularly somatostatin-expressing (SST+) neurons. This claim is supported by the increased density of SST+ neurons found in L4 of the septa compared to barrels, along with a stronger response of (L2/3) SST+ neurons to repeated multi- vs single-whisker stimulation. The role of the synaptic protein Elfn1 is then examined. Elfn1 KO mice exhibited little to no functional domain separation between barrel and septa, with no significant difference in single- versus multi-whisker response ratios across barrel and septal domains. Consistently, a decoder trained on WT data fails to generalize to Elfn1 KO responses. Finally, the authors report a relative enrichment of S2- and M1-projecting cell densities in L4 of the septal domain compared to the barrel domain.

Strengths:

This paper describes and aims to study a circuit underlying differential response between barrel columns and septal domains of the primary somatosensory cortex. This work supports the view that barrel and septal domains contribute differently to processing single versus multi-whisker inputs, suggesting that the barrel cortex multiplexes sensory information coming from the whiskers in different domains.

We thank the reviewer for the very neat summary of our findings that barrel cortex multiplexes converging information in separate domains.

Weaknesses:

While the observed divergence in responses to repeated SWS vs MWS between the barrel and septal domains is intriguing, the presented evidence falls short of demonstrating that short-term plasticity in SST+ neurons critically underpins this difference. The absence of a mechanistic explanation for this observation limits the work’s significance. The measurement of SST neurons’ response is not specific to a particular domain, and the Elfn1 manipulation does not seem to be specific to either stimulus type or a particular domain.

We appreciate the reviewer’s perspective. Although further research is needed to understand the circuit mechanisms underlying the observed phenomenon, we believe our data suggest that altering the short-term dynamics of excitatory inputs onto SST neurons reduces the divergent spiking dynamics in barrels versus septa during repetitive single- and multi-whisker stimulation. Future work could examine how SST neurons, whose somata reside in barrels and septa, respond to different whisker stimuli and the circuits in which they are embedded. At this time, however, the authors believe there is no alternative way to test how the short-term dynamics of excitatory inputs onto SST neurons, as a whole, contribute to the temporal aspects of barrel versus septa spiking.

The study's reach is further constrained by the fact that results were obtained in anesthetized animals, which may not generalize to awake states.

We appreciate the reviewer’s concern regarding the generalizability of our findings from anesthetized animals to awake states. Anesthesia was employed to ensure precise individual whisker stimulation (and multi-whisker in the same animal), which is challenging in awake rodents due to active whisking. While anesthesia may alter higher-order processing, core mechanisms, such as short and long term plasticity in the barrel cortex, are preserved under anesthesia (Martin-Cortecero et al., 2014; Mégevand et al., 2009).

The statistical analysis appears inappropriate, with the use of repeated independent tests, dramatically boosting the false positive error rate.

Thank you for your feedback on our analysis using independent rank-based tests for each time point in wild-type (WT) animals. To address concerns regarding multiple comparisons and temporal dependencies (for Figure 1F and 4D for now but we will add more in our revision), we performed a repeated measures ANOVA for WT animals (13 Barrel, 8 Septa, 20 time points), which revealed a significant main effect of Condition (F(1,19) = 16.33, p < 0.001) and a significant Condition-Time interaction (F(19,361) = 2.37, p = 0.001). Post-hoc tests confirmed significant differences between Barrel and Septa at multiple time points (e.g., p < 0.0025 at times 3, 4, 6, 7, 8, 10, 11, 12, 16, 19 after Bonferroni posthoc correction), supporting a differential multi-whisker vs. single-whisker ratio response in WT animals. In contrast, a repeated measures ANOVA for knock-out (KO) animals (11 Barrel, 7 Septa, 20 time points) showed no significant main effect of Condition (F(1,14) = 0.17, p = 0.684) or Condition-Time interaction (F(19,266) = 0.73, p = 0.791), indicating that the BarrelSepta difference observed in WT animals is absent in KO animals.

Furthermore, the manuscript suffers from imprecision; its conclusions are occasionally vague or overstated. The authors suggest a role for SST+ neurons in the observed divergence in SWS/MWS responses between barrel and septal domains. However, this remains speculative, and some findings appear inconsistent. For instance, the increased response of SST+ neurons to MWS versus SWS is not confined to a specific domain. Why, then, would preferential recruitment of SST+ neurons lead to divergent dynamics between barrel and septal regions? The higher density of SST+ neurons in septal versus barrel L4 is not a sufficient explanation, particularly since the SWS/MWS response divergence is also observed in layers 2/3, where no difference in SST+ neuron density is found.

Moreover, SST+ neuron-mediated inhibition is not necessarily restricted to the layer in which the cell body resides. It remains unclear through which differential microcircuits (barrel vs septum) the enhanced recruitment of SST+ neurons could account for the divergent responses to repeated SWS versus MWS stimulation.

We fully appreciate the reviewer’s comment. We currently do not provide any evidence on the contribution of SST neurons in the barrels versus septa in layer 4 on the response divergence of spiking observed in SWS versus MWS. We only show that these neurons differentially distribute in the two domains in this layer. It is certainly known that there is molecular and circuit-based diversity of SST-positive neurons in different layers of the cortex, so it is plausible that this includes cells located in the two domains of vS1, something which has not been examined so far. Our data on their distribution are one piece of information that SST neurons may have a differential role in inhibiting barrel stellate cells versus septa ones. Morphological reconstructions of SST neurons in L4 of the somatosensory barrel cortex has shown that their dendrites and axons project locally and may confine to individual domains, even though not specifically examined (Fig. 3 of Scala F et al., 2019). The same study also showed that L4 SST cells receive excitatory input from local stellate cells) and is known that they are also directly excited by thalamocortical fibers (Beierlein et al., 2003; Tan et al., 2008), both of which facilitate.

As shown in our supplementary figure, the divergence is also observed in L2/3 where, as the reviewer also points out, where we do not have a differential distribution of SST cells, at least based on a columnar analysis extending from L4. There are multiple scenarios that could explain this “discrepancy” that one would need to examine further in future studies. One straightforward one is that the divergence in spiking in L2/3 domains may be inherited from L4 domains, where L4 SST act on. Another is that even though L2/3 SST neurons are not biased in their distribution their input-output function is, something which one would need to examine by detailed in vitro electrophysiological and perhaps optogenetic approaches in S1. Despite the distinctive differences that have been found between the L4 circuitry in S1 and V1 (Scala F et al., 2019), recent observations indicate that small but regular patches of V1 marked by the absence of muscarinic receptor 2 (M2) have high temporal acuity (Ji et al., 2015), and selectively receive input from SST interneurons (Meier et al., 2025). Regions lacking M2 have distinct input and output connectivity patterns from those that express M2 (Meier et al., 2021; Burkhalter et al., 2023). These findings, together with ours, suggest that SST cells preferentially innervate and regulate specific domains columns- in sensory cortices.

Regardless of the mechanism, the Elfn1 knock-out mouse line almost exclusively affects the incoming excitability onto SST neurons (see also reply to comment below), hence what can be supported by our data is that changing the incoming short-term synaptic plasticity onto these neurons brings the spiking dynamics between barrels and septa closer together.

The Elfn1 KO mouse model seems too unspecific to suggest the role of the short-term plasticity in SST+ neurons in the differential response to repeated SWS vs MWS stimulation across domains. Why would Elfn1-dependent short-term plasticity in SST+ neurons be specific to a pathway, or a stimulation type (SWS vs MWS)? Moreover, the authors report that Elfn1 knockout alters synapses onto VIP+ as well as SST+ neurons (Stachniak et al., 2021; previous version of this paper)-so why attribute the phenotype solely to SST+ circuitry? In fact, the functional distinctions between barrel and septal domains appear largely abolished in the Elfn1 KO.

Previous work by others and us has shown that globally removing Elfn1 selectively removes a synaptic process from the brain without altering brain anatomy or structure. This allows us to study how the temporal dynamics of inhibition shape activity, as opposed to inhibition from particular cell types. We will nevertheless update the text to discuss more global implications for SST interneuron dynamics and include a reference to VIP interneurons that contain Elfn1.

When comparing SWS to MWS, we find that MWS replaces the neighboring excitation which would normally be preferentially removed by short-term plasticity in SST interneurons, thus providing a stable control comparison across animals and genotypes. On average, VIP interneurons failed to show modulation by MWS. We were unable to measure a substantial contribution of VIP cells to this process and also note that the Elfn1 expressing multipolar neurons comprise only ~5% of VIP neurons (Connor and Peters, 1984; Stachniak et al., 2021), a fraction that may be lost when averaging from 138 VIP cells. Moreover, the effect of Elfn1 loss on VIP neurons is quite different and marginal compared to that of SST cells, suggesting that the primary impact of Elfn1 knockout is mediated through SST+ interneuron circuitry. Therefore, even if we cannot rule out that these 5% of VIP neurons contribute to barrel domain segregation, we are of the opinion that their influence would be very limited if any.

Reviewer #2 (Public Reviews):

Summary:

Argunsah and colleagues demonstrate that SST-expressing interneurons are concentrated in the mouse septa and differentially respond to repetitive multi-whisker inputs. Identifying how a specific neuronal phenotype impacts responses is an advance.

Strengths:

(1)  Careful physiological and imaging studies.

(2)  Novel result showing the role of SST+ neurons in shaping responses.

(3)  Good use of a knockout animal to further the main hypothesis.

(4)  Clear analytical techniques.

We thank the reviewer for their appreciation of the study.

Weaknesses:

No major weaknesses were identified by this reviewer. Overall, I appreciated the paper but feel it overlooked a few issues and had some recommendations on how additional clarifications could strengthen the paper. These include:

(1) Significant work from Jerry Chen on how S1 neurons that project to M1 versus S2 respond in a variety of behavioral tasks should be included (e.g. PMID: 26098757). Similarly, work from Barry Connor’s lab on intracortical versus thalamocortical inputs to SST neurons, as well as excitatory inputs onto these neurons (e.g. PMID: 12815025) should be included.

We thank the reviewer for these valuable resources that we overlooked. We will include Chen et al. (2015), Cruikshank et al. (2007) and Gibson et al. (1999) to contextualize S1 projections and SST+ inputs, strengthening the study’s foundation as well as Beierlein et al. (2003) which nicely show both local and thalamocortical facilitation of excitatory inputs onto L4 SST neurons, in contrast to PV cells. The paper also shows the gradual recruitment of SST neurons by thalamocortical inputs to provide feed-forward inhibition onto stellate cells (regular spiking) of the barrel cortex L4 in rat.

(2) Using Layer 2/3 as a proxy to what is happening in layer 4 (~line 234). Given that layer 2/3 cells integrate information from multiple barrels, as well as receiving direct VPm thalamocortical input, and given the time window that is being looked at can receive input from other cortical locations, it is not clear that layer 2/3 is a proxy for what is happening in layer 4.

We agree with the reviewer that what we observe in L2/3 is not necessarily what is taking place in L4 SST-positive cells. The data on L2/3 was included to show that these cells, as a population, can show divergent responses when it comes to SWS vs MWS, which is not seen in L2/3 VIP neurons. Regardless of the mechanisms underlying it, our overall data support that SST-positive neurons can change their activation based on the type of whisker stimulus and when the excitatory input dynamics onto these neurons change due to the removal of Elfn1 the recruitment of barrels vs septa spiking changes at the temporal domain. Having said that, the data shown in Supplementary Figure 3 on the response properties of L2/3 neurons above the septa vs above the barrels (one would say in the respective columns) do show the same divergence as in L4. This suggests that a circuit motif may exist that is common to both layers, involving SST neurons that sit in L4, L5 or even L2/3. This implies that despite the differences in the distribution of SST neurons in septa vs barrels of L4 there is an unidentified input-output spatial connectivity motif that engages in both L2/3 and L4. Please also see our response to a similar point raised by reviewer 1.

(3) Line 267, when discussing distinct temporal response, it is not well defined what this is referring to. Are the neurons no longer showing peaks to whisker stimulation, or are the responses lasting a longer time? It is unclear why PV+ interneurons which may not be impacted by the Elfn1 KO and receive strong thalamocortical inputs, are not constraining activity.

We thank the reviewer for their comment and will clarify the statement.

This convergence of response profiles was further clear in stimulus-aligned stacked images, where the emergent differences between barrels and septa under SWS were largely abolished in the KO (Figure 4B). A distinction between directly stimulated barrels and neighboring barrels persisted in the KO. In addition, the initial response continued to differ between barrel and septa and also septa and neighbor (Figure 4B). This initial stimulus selectivity potentially represents distinct feedforward thalamocortical activity, which includes PV+ interneuron recruitment that is not directly impacted by the Elfn1 KO (Sun et al., 2006; Tan et al., 2008). PV+ cells are strongly excited by thalamocortical inputs, but these exhibit short-term depression, as does their output, contrasting with the sustained facilitation observed in SST+ neurons. These findings suggest that in WT animals, activity spillover from principal barrels is normally constrained by the progressive engagement of SST+ interneurons in septal regions, driven by Elfn1-dependent facilitation at their excitatory synapses. In the absence of Elfn1, this local inhibitory mechanism is disrupted, leading to longer responses in barrels, delayed but stronger responses in septa, and persistently stronger responses in unstimulated neighbors, resulting in a loss of distinction between the responses of barrel and septa domains that normally diverge over time (see Author response image 1 below).

Author response image 1.

(A) Barrel responses are longer following whisker stimulation in KO. (B) Septal responses are slightly delayed but stronger in KO. (C) Unstimulated neighbors show longer persistent responses in KO.

(4) Line 585 “the earliest CSD sink was identified as layer 4…” were post-hoc measurements made to determine where the different shank leads were based on the post-hoc histology?

Post hoc histology was performed on plane-aligned brain sections which would allow us to detect barrels and septa, so as to confirm the insertion domains of each recorded shank. Layer specificity of each electrode therefore could therefore not be confirmed by histology as we did not have coronal sections in which to measure electrode depth.

(5) For the retrograde tracing studies, how were the M1 and S2 injections targeted (stereotaxically or physiologically)? How was it determined that the injections were in the whisker region (or not)?

During the retrograde virus injection, the location of M1 and S2 injections was determined by stereotaxic coordinates (Yamashita et al., 2018). After acquiring the light-sheet images, we were able to post hoc examine the injection site in 3D and confirm that the injections were successful in targeting the regions intended. Although it would have been informative to do so, we did not functionally determine the whisker-related M1 and whisker-related S2 region in this experiment.

(6) Were there any baseline differences in spontaneous activity in the septa versus barrel regions, and did this change in the KO animals?

Thank you for this interesting question. Our previous study found that there was a reduction in baseline activity in L4 barrel cortex of KO animals at postnatal day (P)12, but no differences were found at P21 (Stachniak et al., 2023).

Reviewer #3 (Public Reviews):

Summary:

This study investigates the functional differences between barrel and septal columns in the mouse somatosensory cortex, focusing on how local inhibitory dynamics, particularly involving Elfn1-expressing SST⁺ interneurons, may mediate temporal integration of multiwhisker (MW) stimuli in septa. Using a combination of in vivo multi-unit recordings, calcium imaging, and anatomical tracing, the authors propose that septa integrate MW input in an Elfn1-dependent manner, enabling functional segregation from barrel columns.

Strengths:

The core hypothesis is interesting and potentially impactful. While barrels have been extensively characterized, septa remain less understood, especially in mice, and this study's focus on septal integration of MW stimuli offers valuable insights into this underexplored area. If septa indeed act as selective integrators of distributed sensory input, this would add a novel computational role to cortical microcircuits beyond what is currently attributed to barrels alone. The narrative of this paper is intellectually stimulating.

We thank the reviewer for finding the study intellectually stimulating.

Weaknesses:

The methods used in the current study lack the spatial and cellular resolution needed to conclusively support the central claims. The main physiological findings are based on unsorted multi-unit activity (MUA) recorded via low-channel-count silicon probes. MUA inherently pools signals from multiple neurons across different distances and cell types, making it difficult to assign activity to specific columns (barrel vs. septa) or neuron classes (e.g., SST⁺ vs. excitatory).

The recording radius (~50-100 µm or more) and the narrow width of septa (~50-100 µm or less) make it likely that MUA from "septal" electrodes includes spikes from adjacent barrel neurons.

The authors do not provide spike sorting, unit isolation, or anatomical validation that would strengthen spatial attribution. Calcium imaging is restricted to SST⁺ and VIP⁺ interneurons in superficial layers (L2/3), while the main MUA recordings are from layer 4, creating a mismatch in laminar relevance.

We thank the reviewer for pointing out the possibility of contamination in septal electrodes. Importantly, it may not have been highlighted, although reported in the methods, but we used an extremely high threshold (7.5 std, in methods, line 583) for spike detection in order to overcome the issue raised here, which restricts such spatial contaminations. Since the spike amplitude decays rapidly with distance, at high thresholds, only nearby neurons contribute to our analysis, potentially one or two. We believe that this approach provides a very close approximation of single unit activity (SUA) in our reported data. We will include a sentence earlier in the manuscript to make this explicit and prevent further confusion.

Regarding the point on calcium imaging being performed on L2/3 SST and VIP cells instead of L4. Both reviewer 1 and 2 brought up the same issue and we responded as follows. As shown in our supplementary figure, the divergence is also observed in L2/3 where we do not have a differential distribution of SST cells, at least based on a columnar analysis extending from L4. There are multiple scenarios that could explain this “discrepancy” that one would need to examine further in future studies. One straightforward one is that the divergence in spiking in L2/3 domains may be inherited from L4 domains, where L4 SST act on. Another is that even though L2/3 SST neurons are not biased in their distribution their input-output function is, something which one would need to examine by detailed in vitro electrophysiological and perhaps optogenetic approaches in S1. Despite the distinctive differences that have been found between the L4 circuitry in S1 and V1 (Scala F et al., 2019), recent observations indicate that small but regular patches of V1 marked by the absence of muscarinic receptor 2 (M2) have high temporal acuity (Ji et al., 2015), and selectively receive input from SST interneurons (Meier et al., 2025). Regions lacking M2 have distinct input and output connectivity patterns from those that express M2 (Meier et al., 2021; Burkhalter et al., 2023). These findings, together with ours, suggest that SST cells preferentially innervate and regulate specific domains -columns- in sensory cortices.

Furthermore, while the role of Elfn1 in mediating short-term facilitation is supported by prior studies, no new evidence is presented in this paper to confirm that this synaptic mechanism is indeed disrupted in the knockout mice used here.

We thank Reviewer #3 for noting the absence of new evidence confirming Elfn1’s disruption of short-term facilitation in our knockout mice. We acknowledge that our study relies on previously strong published data demonstrating that Elfn1 mediates short-term synaptic facilitation of excitatory inputs onto SST+ interneurons (Sylwestrak and Ghosh, 2012; Tomioka et al., 2014; Stachniak et al., 2019, 2023). These studies consistently show that Elfn1 knockout abolishes facilitation in SST+ synapses, leading to altered temporal dynamics, which we hypothesize underlies the observed loss of barrel-septa response divergence in our Elfn1 KO mice (Figure 4). Nevertheless, to address the point raised, we will clarify in the revised manuscript (around lines 245-247 and 271-272) that our conclusions are based on these established findings, stating: “Building on prior evidence that Elfn1 knockout disrupts short-term facilitation in SST+ interneurons (Sylwestrak and Ghosh, 2012; Tomioka et al., 2014; Stachniak et al., 2019, 2023), we attribute the abolished barrel-septa divergence in Elfn1 KO mice to altered SST+ synaptic dynamics, though direct synaptic measurements were not performed here.”

Additionally, since Elfn1 is constitutively knocked out from development, the possibility of altered circuit formation-including changes in barrel structure and interneuron distribution, cannot be excluded and is not addressed.

We thank Reviewer #3 for raising the valid concern that constitutive Elfn1 knockout could potentially alter circuit formation, including barrel structure and interneuron distribution. To address this, we will clarify in the revised manuscript (around line ~271 and in the Discussion) that in our previous studies that included both whole-cell patch-clamp in acute brain slices ranging from postnatal day 11 to 22 (P11 - P21) and in vivo recordings from barrel cortex at P12 and P21, we saw no gross abnormalities in barrel structure, with Layer 4 barrels maintaining their characteristic size and organization, consistent with wildtype (WT) mice (Stachniak et al., 2019, 2023). While we cannot fully exclude subtle developmental changes, prior studies indicate that Elfn1 primarily modulates synaptic function rather than cortical cytoarchitecture (Tomioka et al., 2014). Elfn1 KO mice show no gross morphological or connectivity differences and the pattern and abundance of Elfn1 expressing cells (assessed by LacZ knock in) appears normal (Dolan and Mitchell, 2013).

We will add the following to the Discussion: “Although Elfn1 is constitutively knocked out, we find here and in previous studies that barrel structure is preserved (Stachniak et al., 2019, 2023). Further, the distribution of Elfn1 expressing interneurons is not different in KO mice, suggesting minimal developmental disruption (Dolan and Mitchell, 2013).

Nonetheless, we acknowledge that subtle circuit changes cannot be ruled out without the usage of time-depended conditional knockout of the gene.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) My biggest concern is regarding statistics. Did the authors repeatedly apply independent tests (Mann-Whitney) without any correction for multiple comparisons (Figures 1 and 4)? In that case, the chances of a spurious "significant" result rise dramatically. 

In response to the reviewer’s comment, we now present new statistical results by utilizing ANOVA and blended these results in the manuscript between lines 172 and 192 for WT data and 282 and 298 for Elfn1 KO data. This new statistical approach shows the same differences as we had previously reported, hence consolidating the statements made. 

(2) The findings only hint at a mechanism involving SST+ neurons for how SWS and MWS are processed differently in the barrel vs septal domains. As a direct test of SST+ neuron involvement in the divergence of barrel and septal responses, the authors might consider SST-specific manipulations - for example, inhibitory chemo- or optogenetics during SWS and MWS stimulation.

We thank the reviewer for this comment and agree that a direct manipulation of SST+ neurons via inhibitory chemo- or opto-genetics could provide further supporting evidence for the main claims in our study. We have opted out from performing these experiments for this manuscript as we feel they can be part of a future study.  At the same time, it is conceivable that such manipulations and depending on how they are performed may lead to larger and non-specific effects on cortical activity, since SST neurons will likely be completely shut down. So even though we certainly appreciate and value the strengths of such approaches, our experiments have addressed a more nuanced hypothesis, namely that the synaptic dynamics onto SST+ neurons matter for response divergence of septa versus barrels, which could not have been easily and concretely addressed by manipulating SST+ cell firing activity.  

(3) In general, it is hard to comprehend what microcircuit could lead to the observed divergence in the MWS/SWS ratio in the barrel vs septal domain. There preferential recruitment of SST+ neurons during MWS is not specific to a particular domain, and the higher density of SST+ neurons specifically in L4 septa cannot per se explain the diverging MWS/SWS ratio in L4 septal neurons since similar ratio divergence is observed across domains in L2/3 neurons without increase SST+ neuron density in L2/3. This view would also assume that SST+ inhibition remains contained to its own layer and domain. Is this the case? Is it that different microcircuits between barrels and septa differently shape the response to repeated MWS? This is partially discussed in the paper; can the authors develop on that? What would the proposed mechanism be? Can the short-term plasticity of the thalamic inputs (VPM vs POm) be part of the picture?

We thank the reviewer for raising this important point. We propose that the divergence in MWS/SWS ratios across barrel and septal domains arises from dynamic microcircuit interactions rather than static anatomical features such as SST+ density, which we describe and can provide a hint. In L2/3, where SST+ density is uniform, divergence persists, suggesting that trans-laminar and trans-domain interactions are key. Barrel domains, primarily receiving VPM inputs, exhibit short-term depression onto excitatory cells and engage PV+ and SST+ neurons to stabilize the MWS/SWS ratio, with Elfn1-dependent facilitation of SST+ neurons gradually increasing inhibition during repetitive SWS. Septal domains, in contrast, are targeted by facilitating POm inputs, combined with higher L4 SST+ density and Elfn1-mediated facilitation, producing progressive inhibitory buildup that amplifies the MWS/SWS ratio. SST+ projections in septa may extend trans-laminarly and laterally, influencing L2/3 and neighboring barrels, thereby explaining L2/3 divergence despite uniform SST+ density in L2/3. In this regards, direct laminar-dependent manipulations will be required to confirm whether L2/3 divergence is inherited from L4 dynamics. In Elfn1 KO mice, the loss of facilitation in SST+ neurons likely flattens these dynamics, disrupting functional segregation. Future experiments using VPM/POm-specific optogenetic activation and SST+ silencing will be critical to directly test this model.

We expanded the discussion accordingly.

(4) Can the decoder generalize between SWS and MWS? In this condition, if the decoder accuracy is higher for barrels than septa, it would support the idea that septa are processing the two stimuli differently. 

Our results show that septal decoding accuracy is generally higher than barrel accuracy when generalizing from multi-whisker stimulation (MWS) to single-whisker stimulation (SWS), indicating distinct information processing in septa compared to barrels.

In wild-type (WT) mice, septal accuracy exceeds barrel accuracy across all time windows (150ms, 51-95ms, 1-95ms), with the largest difference in the 51-95ms window (0.9944 vs. 0.9214 at pulse 20, 10Hz stimulation). This septal advantage grows with successive pulses, reflecting robust, separable neural responses, likely driven by the posterior medial nucleus (POm)’s strong MWS integration contrasting with minimal SWS activation. Barrel responses, driven by consistent ventral posteromedial nucleus (VPM) input for both stimuli, are less distinguishable, leading to lower accuracy.

In Elfn1 knockout (KO) mice, which disrupt excitatory drive to somatostatin-positive (SST+) interneurons, barrel accuracy is higher initially in the 1-50ms window (0.8045 vs. 0.7500 at pulse 1), suggesting reduced early septal distinctiveness. However, septal accuracy surpasses barrels in later pulses and time windows (e.g., 0.9714 vs. 0.9227 in 51-95ms at pulse 20), indicating restored septal processing. This supports the role of SST+ interneurons in shaping distinct MWS responses in septa, particularly in late-phase responses (51-95ms), where inhibitory modulation is prominent, as confirmed by calcium imaging showing stronger SST+ activation during MWS.

These findings demonstrate that septa process SWS and MWS differently, with higher decoding accuracy reflecting structured, POm- and SST+-driven response patterns. In Elfn1 KO mice, early deficits in septal processing highlight the importance of SST+ interneurons, with later recovery suggesting compensatory mechanisms. 

We have added Supplementary Figure 4 and included this interpretation between lines 338353. 

We thank the reviewer for suggesting this analysis.

(5) It is not clear to me how the authors achieve SWS. How is it that the pipette tip "placed in contact with the principal whisker" does not detach from the principal whisker or stimulate other whiskers? Please clarify the methods. 

Targeting the specific principal whisker is performed under the stereoscope.  

Specifically, we have added this statement in line 628:

“We trimmed the whiskers where necessary, to avoid them touching each other and to avoid stimulating other whiskers. By putting the pipette tip very close (almost touching) to the principal whisker, the movement of the tip (limited to 1mm) would reliably move the targeted whisker. The specificity of the stimulation of the selected principal whisker was observed under the stereoscope.”

(6) The method for calculating decoder accuracy is not clearly described-how can accuracy exceed 1? The authors should clarify this metric and provide measures of variability (e.g., confidence intervals or standard deviations across runs) to assess the significance of their comparisons. Additionally, using a consistent scale across all plots would improve interoperability. 

We thank the reviewer for raising this point. We have now changed the way accuracies are calculated and adopted a common scale among different plots (see updated Figure 5). We have also changed the methods section accordingly.

(7) Figure 1: The sample size is not specified. It looks like the numbers match the description in the methods, but the sample size should be clearly stated here. 

These are the numbers the reviewer is inquiring about. 

WT: (WT) animals: a 280 × 95 × 20 matrix for the stimulated barrel (14 Barrels, 95ms, 20 pulses), a 180 × 95 × 20 matrix for the septa (9 Septa, 95ms, 20 pulses), and a 360 × 95 × 20 matrix for the neighboring barrel (18 Neighboring barrels, 95ms, 20 pulses). N=4 mice.

KO: 11-barrel columns, 7 septal columns, 11 unstimulated neighbors from N=4 mice.

Panels D-F are missing axes and axis labels (firing rate, p-value). Panel D is mislabeled (left, middle, and right). I can't seem to find the yellow line. 

Thank you for this observation. We made changes in the figures to make them easier to navigate based on the collective feedback from the reviewers.

Why is changing the way to compare the differences in the responses to repeated stimulation between SWS and MWS? 

To assess temporal accumulation of information, we compared responses to repeated single-whisker stimulation (SWS) and multi-whisker stimulation (MWS) using an accumulative decoding approach rather than simple per-pulse firing rates. This method captures domain-specific integration dynamics over successive pulses.

The use of the term "principal whisker" is confusing, as it could refer to the whisker that corresponds to the recorded barrel. 

When we use the term principal whisker, the intention is indeed to refer to the whisker corresponding to the recorded barrel during single whisker stimulation. The term principal whisker is removed from Figure legend 1 and legend S1C where it may have led to  ambiguity.    

Why the statement "after the start of active whisking"? Mice are under anesthesia here; it does not appear to be relevant for the figure. 

“After the start of active whisking” refers to the state of the barrel cortex circuitry at the time of recordings. The particular reference we use comes from the habit of assessing sensory processing also from a developmental point of view. The reviewer is correct that it has nothing to do the with the status of the experiment. Nevertheless, since the reviewer found that it may create confusion, we have now taken it out. 

(8) Figure 3: The y-axis label is missing for panel C. 

This is now fixed. (dF/F).

(9) Figure 4: Axis labels are missing.

Added.

Minor: 

(10) Line 36: "progressive increase in septal spiking activity upon multi-whisker stimulation". There is no increase in septal spiking activity upon MWS; the ratio MWS/SWS increases.

We have changed the sentence as follows: Genetic removal of Elfn1, which regulates the incoming excitatory synaptic dynamics onto SST+ interneurons, leads to the loss of the progressive increase in septal spiking ratio (MWS/SWS) upon stimulation.

(11) Line 105: domain-specific, rather than column-specific, for consistency.

We have changed it.

(12) Lines 173-174: "a divergence between barrel and septa domain activity also occurred in Layer 4 from the 2nd pulse onward (Figure 1E)". The authors only show a restricted number of comparisons. Why not show the p-values as for SWS?

The statistics is now presented in current Figure 1E.

(13) Lines 151-153: "Correspondingly, when a single whisker is stimulated repeatedly, the response to the first pulse is principally bottom-up thalamic-driven responses, while the later pulses in the train are expected to also gradually engage cortico-thalamo-cortical and cortico-cortical loops." Can the authors please provide a reference?

We have now added the following references : (Kyriazi and Simons, 1993; Middleton et al., 2010; Russo et al., 2025).

(14) Lines 184-186: "Our electrophysiological experiments show a significant divergence of responses over time upon both SWS and MWS in L4 between barrels (principal and neighboring) and adjacent septa, with minimal initial difference". The only difference between the neighboring barrel and septa is the responses to the initial pulse. Can the author clarify? 

We have now changed the sentence as follows: Our electrophysiological experiments show a significant divergence of responses between domains upon both SWS and MWS in L4. (Line 198 now)

(15) Line 214: "suggest these interneurons may play a role in diverging responses between barrels and septa upon SWS". Why SWS specifically?

We have changed the sentence as follows: These results confirmed that SST+ and VIP+ interneurons have higher densities in septa compared to barrels in L4 and suggest these interneurons may play a role in diverging responses between barrels and septa. (Line 231 now).

(16) Line 235: "This result suggests that differential activation of SST+ interneurons is more likely to be involved in the domain-specific temporal ratio differences between barrels and septa". Why? The results here are not domain-specific.

We have now revised this statement to: This result suggested that temporal ratio differences specific to barrels and septa might involve differential activation of SST+ interneurons rather than VIP+ interneurons.

(17) Lines 241-243: "SST+ interneurons in the cortex are known to show distinct short-term synaptic plasticity, particularly strong facilitation of excitatory inputs, which enables them to regulate the temporal dynamics of cortical circuits." Please provide a reference.

We have now added the following references: (Grier et al., 2023; Liguz-Lecznar et al., 2016).

(18) Lines 245-247: "A key regulator of this plasticity is the synaptic protein Elfn1, which mediates short-term synaptic facilitation of excitation on SST+ interneurons (Stachniak et al., 2021, 2019; Tomioka et al., 2014)". Is Stachniak et al., 2021 not about the role of Elf1n in excitatory-to-VIP+ neuron synapses?

The reviewer correctly spotted this discrepancy . This reference has now been removed from this statement.

(19) Lines 271-272: "Building on our findings that Elfn1-dependent facilitation in SST+ interneurons is critical for maintaining barrel-septa response divergence". The authors did not show that.

We have now changed the statement to: Building on our findings that Elfn1 is critical for maintaining barrel-septa response divergence  

(20) Line 280: second firing peak, not "peal".

Thank you, it is now fixed.

(21) Lines 304-305: "These results highlight the critical role of Elfn1 in facilitating the temporal integration of 305 sensory inputs through its effects on SST+ interneurons". This claim is also overstated. 

We have now changed the statement to: These results highlight the contribution of Elfn1 to the temporal integration of sensory inputs. (Line 362)

(22) Line 329: Any reason why not cite Chen et al., Nature 2013?

We have now added this reference, as also pointed out by reviewer 1.

(23) Line 341-342: "wS1" and "wS2" instead of S1 and S2 for consistency.

Thanks, we have now updated the terms.

Reviewer #2 (Recommendations for the authors): 

(1) Figure 3D - the SW conditions are labeled but not the MW conditions (two right graphs) - they should be labeled similarly (SSTMW, VIPMW). 

The two right graphs in Figure 3D represent paired SW vs MW comparisons of the evoked responses for SST and VIP populations, respectively.

(2) Figure 6 D and E I think it would be better if the Depth measurements were to be on the yaxis, which is more typical of these types of plots. 

We thank the reviewer for this comment. Although we appreciate this may be the case, we feel that the current presentation may be easier for the reader to navigate, and we have hence kept it. 

(3) Having an operational definition of septa versus barrel would be useful. As the authors point out, this is a tough distinction in a mouse, and often you read papers that use Barrel Wall versus Barrel Hollow/Center - operationally defining how these areas were distinguished would be helpful. 

We thank the reviewer for this comment and understand the point made.

We have now updated the methods section in line 611: 

DiI marks contained within the vGlut2 staining were defined as barrel recordings, while DiI marks outside vGlut2 staining were septal recordings.

Reviewer #3 (Recommendations for the authors): 

To support the manuscript's major claims, the authors should consider the following:

(1) Validate the septal identity of the neurons studied, either anatomically or functionally at the single-cell level (e.g., via Ca²⁺ imaging with confirmed barrel/septa mapping). 

We thank the reviewer for this suggestion, but we feel that these extensive experiments are beyond the scope of this study. 

(2) Provide both anatomical and physiological evidence to assess the possibility of altered cortical development in Elfn1 KO mice, including potential changes in barrel structure or SST⁺ cell distribution. 

To address the reviewer’s point, we have now added the following to the Discussion: “Although Elfn1 is constitutively knocked out, we find here and in previous studies that barrel structure is preserved (Stachniak et al., 2019, 2023). Further, the distribution of Elfn1 expressing interneurons is not different in KO mice, suggesting minimal developmental disruption (Dolan and Mitchell, 2013). Nonetheless, we acknowledge that subtle circuit changes cannot be ruled out without conditional knockouts.”,

(3) Examine the sensory responses of SST⁺ and VIP⁺ interneurons in deeper cortical layers, particularly layer 4, which is central to the study's main conclusions.

We thank the reviewer for this suggestion and appreciate the value it would bring to the study. We nevertheless feel that these extensive experiments are beyond the scope of this study and hence opted out from performing them. 

Minor Comments:

(1)  The authors used a CLARITY-based passive clearing protocol, which is known to sometimes induce tissue swelling or distortion. This may affect anatomical precision, especially when assigning neurons to narrow domains such as septa versus barrels. Please clarify whether tissue expansion was measured, corrected, or otherwise accounted for during analysis.

Yes, the tissue expansion was accounted during analysis for the laminar specification. We excluded the brains with severe distortion. 

(2) While the anatomical data are plotted as a function of "depth from the top of layer 4," the manuscript does not specify the precise depth ranges used to define individual cortical layers in the cleared tissue. Given the importance of laminar specificity in projection and cell type analyses, the criteria and boundaries used to delineate each layer should be explicitly stated.

Thank you for pointing this out. We now include the criteria for delineating each layer in the manuscript. “Given that the depth of Layer 4 (L4) can be reliably measured due to its welldefined barrel boundaries, and that the relative widths of other layers have been previously characterized (El-Boustani et al., 2018), we estimated laminar boundaries proportionally. Specifically, Layer 2/3 was set to approximately 1.3–1.5 times the width of L4, Layer 5a to ~0.5 times, and Layer 5b to a similar width as L4. Assuming uniform tissue expansion across the cortical column, we extrapolated the remaining laminar thicknesses proportionally.”

(3)  In several key comparisons (e.g., SST⁺ vs. VIP⁺ interneurons, or S2-projecting vs. M1projecting neurons), it is unclear whether the same barrel columns were analyzed across conditions. Given the anatomical and functional heterogeneity across wS1 columns, failing to control for this may introduce significant confounds. We recommend analyzing matched columns across groups or, if not feasible, clearly acknowledging this limitation in the manuscript.

We thank the reviewer for raising this important point. For the comparison of SST⁺ versus VIP⁺ interneurons, it would in principle have been possible to analyze the same barrel columns across groups. However, because some of the cleared brains did not reach the optimal level of clarity, our choice of columns was limited, and we were not always able to obtain sufficiently clear data from the same columns in both groups. Similarly, for the analysis of S2- versus M1-projecting neurons, variability in the position and spread of retrograde virus injections made it difficult to ensure measurements from identical barrel columns. We have now added a statement in the Discussion to acknowledge this limitation.

(4) Figure 1C: Clarify what each point in the t-SNE plot represents-e.g., a single trial, a recording channel, or an averaged response. Also, describe the input features used for dimensionality reduction, including time windows and preprocessing steps.

In response to the reviewer’s comment, we have now added the following in the methods: In summary, each point in the t-SNE plots represents an averaged response across 20 trials for a specific domain (barrel, septa, or neighbor) and genotype (WT or KO), with approximately 14 points per domain derived from the 280 trials in each dataset. The input features are preprocessed by averaging blocks of 20 trials into 1900-dimensional vectors (95ms × 20), which are then reduced to 2D using t-SNE with the specified parameters. This approach effectively highlights the segregation and clustering patterns of neural responses across cortical domains in both WT and KO conditions.

(5) Figures 1D, E (left panels): The y-axes lack unit labeling and scale bars. Please indicate whether values are in spikes/sec, spikes/bin, or normalized units.

We have now clarified this. 

(6) Figures 1D, E (right panels): The color bars lack units. Specify whether the values represent raw firing rates, z-scores, or other normalized measures. Replace the vague term "Matrix representation" with a clearer label such as "Pulse-aligned firing heatmap."

Thank you, we have now done it.

(7) Figure 1E (bottom panel): There appears to be no legend referring to these panels. Please define labels such as "B" and "S." 

Thank you, we have now done it.

(8) Figure 1E legend: If it duplicates the legend from Figure 1D, this should be made explicit or integrated accordingly. 

We have changed the structure of this figure.

(9) Figure 1F: Define "AUC" and explain how it was computed (e.g., area under the firing rate curve over 0-50 ms). Indicate whether the plotted values represent percentages and, if so, label the y-axis accordingly. If normalization was applied, describe the procedure. Include sample sizes (n) and specify what each data point represents (e.g., animal, recording site). 

The following paragraph has been added in the methods section:

The Area Under the Curve (AUC) was computed as the integral of the smoothed firing rate (spikes per millisecond) over a 50ms window following each whisker stimulation pulse, using trapezoidal integration. Firing rate data for layer 4 barrel and septal regions in wild-type (WT) and knockout (KO) mice were smoothed with a 3-point moving average and averaged across blocks of 20 trials. Plotted values represent the percentage ratio of multi-whisker (MW) to single whisker (SW) AUC with error bars showing the standard error of the mean. Each data point reflects the mean AUC ratio for a stimulation pulse across approximately 11 blocks (220 trials total). The y-axis indicates percentages.

(10) Figure 3C: Add units to the vertical axis.

We have added them.

(11) Figure 3D: Specify what each line represents (e.g., average of n cells, individual responses?). 

Each line represents an average response of a neuron.  

(12) Figure 4C legend: Same with what?". No legend refers to the bottom panels - please revise to clarify. 

Thank you. We have now changed the figure structure and legends and fixed the missing information issue.

(13) Supplementary Figure 1B: Indicate the physical length of the scale bar in micrometers. 

This has been fixed. The scale bar is 250um.

(14) Indicate the catalog number or product name of the 8×8 silicon probe used for recordings.

We have added this information. It is the A8x8-Edge-5mm-100-200-177-A64

References

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(2) Burkhalter, A., D’Souza, R. D. & Ji, W. (2023). Integration of feedforward and feedback information streams in the modular architecture of mouse visual cortex. Annu. Rev. Neurosci. 46, 259–280.

(3) Chen, J. L., Margolis, D. J., Stankov, A., Sumanovski, L. T., Schneider, B. L. & Helmchen, F. (2015). Pathway-specific reorganization of projection neurons in somatosensory cortex during learning. Nat. Neurosci. 18, 1101–1108.

(4) Connor, J. R. & Peters, A. (1984). Vasoactive intestinal polypeptide-immunoreactive neurons in rat visual cortex. Neuroscience 12, 1027–1044.

(5) Cruikshank, S. J., Lewis, T. J. & Connors, B. W. (2007). Synaptic basis for intense thalamocortical activation of feedforward inhibitory cells in neocortex. Nat. Neurosci. 10, 462–468.

(6) Dolan, J. & Mitchell, K. J. (2013). Mutation of Elfn1 in mice causes seizures and hyperactivity. PLoS One 8, e80491.

(7) Gibson, J. R., Beierlein, M. & Connors, B. W. (1999). Two networks of electrically coupled inhibitory neurons in neocortex. Nature 402, 75–79.

(8) Ji, W., Gămănuţ, R., Bista, P., D’Souza, R. D., Wang, Q. & Burkhalter, A. (2015). Modularity in the organization of mouse primary visual cortex. Neuron 87, 632–643.

(9) Martin-Cortecero, J. & Nuñez, A. (2014). Tactile response adaptation to whisker stimulation in the lemniscal somatosensory pathway of rats. Brain Res. 1591, 27–37.

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Author response:

The following is the authors’ response to the original reviews.

eLife Assessment

This important manuscript provides insights into the competition between Splicing Factor 1 (SF1) and Quaking (QKI) for binding at the ACUAA branch point sequence in a model intron, regulating exon inclusion. The study employs rigorous transcriptomic, proteomic, and reporter assays, with both mammalian cell culture and yeast models. Nevertheless, while the data are convincing, broadening the analysis to additional exons and narrowing the manuscript's title to better align with the experimental scope would strengthen the work.

Public Reviews:

Reviewer #1 (Public review):

In this manuscript, the authors aimed to show that SF1 and QKI compete for the intron branch point sequence ACUAA and provide evidence that QKI represses inclusion when bound to it.

Major strengths of this manuscript include:

(1) Identification of the ACUAA-like motif in exons regulated by QKI and SF1.

(2) The use of the splicing reporter and mutant analysis to show that upstream and downstream ACUAAC elements in intron 10 of RAI are required for repressing splicing.

(3) The use of proteomic to identify proteins in C2C12 nuclear extract that binds to the wild type and mutant sequence.

(4) The yeast studies showing that ectopic lethality when Qki5 expression was induced, due to increased mis-splicing of transcripts that contain the ACUAA element.

The authors conclusively show that the ACUAA sequence is bound by QKI and provide strong evidence that this leads to differences in exons inclusion and exclusion. In animal cells, and especially in human, branchpoint sequences are degenerate but seem to be recognized by specific splicing factors. Although a subset of splicing factors shows tissue-specific expression patterns most don't, suggesting that yet-to-be-identified mechanisms regulate splicing. This work suggests that an alternate mechanism could be related to the binding affinity of specific RNA binding factors for branchpoint sequences coupled with the level of these different splicing factors in a given cell.

We thank the reviewer for the positive comments.

Reviewer #2 (Public review):

Summary:

In this manuscript, Pereira de Castro and coworkers are studying potential competition between a more standard splicing factor SF1, and an alternative splicing factor called QK1. This is interesting because they bind to overlapping sequence motifs and could potentially have opposing effects on promoting the splicing reaction. To test this idea, the authors KD either SF1 or QK1 in mammalian cells and uncover several exons whose splicing regulation follows the predicted pattern of being promoted for splicing by SF1 and repressed by QK1. Importantly, these have introns enriched in SF1 and QK1 motifs. The authors then focus on one exon in particular with two tandem motifs to study the mechanism of this in greater detail and their results confirm the competition model. Mass spec analysis largely agrees with their proposal; however, it is complicated by the apparently quick transition of SF1-bound complexes to later splicing intermediates. An inspired experiment in yeast shows how QK1 competition could potentially have a detrimental impact on splicing in an orthogonal system. Overall, these results show how splicing regulation can be achieved by competition between a "core" and alternative splicing factor and provide additional insight into the complex process of branch site recognition. The manuscript is exceptionally clear and the figures and data are very logically presented. The work will be valuable to those in the splicing field who are interested in both mechanism and bioinformatics approaches to deconvolve any apparent "splicing code" being used by cells to regulate gene expression. Criticisms are minor and the most important of them stem from overemphasis on parts of the manuscript on the evolutionary angle when evolution itself wasn't analyzed per se.

We thank the reviewer for the positive comments and very clear and fair critical points.

Strengths:

(1) The main discovery of the manuscript involving evidence for SF1/QK1 competition is quite interesting and important for this field. This evidence has been missing and may change how people think about branch site recognition.

(2) The experiments and the rationale behind them are exceptionally clearly and logically presented. This was wonderful!

Thank you so much. We felt the overall flow of the paper and data make for a nice “story” that conveys a relatively easy-to-understand explanation for a complex subject.

(3) The experiments are carried out to a high standard and well-designed controls are included.

(4) The extrapolation of the result to yeast in order to show the potentially devastating consequences of the QK1 competition was very exciting and creative.

We agree this is a very exciting result and finding! Thanks.

Weaknesses:

Overall the weaknesses are relatively minor and involve cases where clarification is necessary, some additional analysis could bolster the arguments, and suggestions for focusing the manuscript on its strengths.

(1) The title (Ancient...evolutionary outcomes), abstract, and some parts of the discussion focus heavily on the evolutionary implications of this work. However, evolutionary analysis was not performed in these studies (e.g., when did QK1 and SF1 proteins arise and/or diverge? How does this line up with branch site motifs and evolution of U2? Any insight from recent work from Scott Roy et al?). I think this aspect either needs to be bolstered with experimental work/data or this should be tamped down in the manuscript. I suggest highlighting the idea expressed in the sentence "A nuanced implication of this model is that loss-of-function...". To me, this is better supported by the data and potentially by some analysis of mutations associated with human disease.

We have revised the title and dampened the evolutionary aspects of the previous version of the manuscript.

(2) One paper that I didn't see cited was that by Tanackovic and Kramer (Mol Biol Cell 2005). This paper is relevant because they KD SF1 and found it nonessential for splicing in vivo. Do their results have implications for those here? How do the results of the KD compare? Could QK1 competition have influenced their findings (or does their work influence the "nuanced implication" model referenced above?)?

This is an interesting point, and thank you for the suggestion. We have now included a brief description of this study in the Introduction of the revised manuscript and do note that the authors measured intron retention of a beta globin reporter and SF3A1, SF3A2, and SF3A3 during SF1 knockdown, but did not detect elevated unspliced RNA in these targets.

(3) Can the authors please provide a citation for the statement "degeneracy is observed to a higher degree in organisms with more alternative splicing"? Does recent evolutionary analysis support this?

We have removed the statement, as it did not add much to the content and I am not sure I can state the concept I was attempting to convey in a simple manner with few citations.

(4) For the data in Figure 3, I was left wondering if NMD was confounding this analysis. Can the authors respond to this and address this concern directly?

We have not measured if the reporters used in Figure 3 produce protein(s). Presumably, though, all spliced reporter RNA would be degraded equally (the included/skipped isoforms’ “reading frames” are not altered from one another). This would not be case for unspliced nuclear reporter RNA, however. Given this difference, and that our analysis can not resolve the subcellular localization of the different reporter species, we have removed the measurement of and subsequent results describing unspliced reporter RNA from Figure 3.

(5) To me, the idea that an engaged U2 snRNP was pulled down in Figure 4F would be stronger if the snRNA was detected. Was that able to be observed by northern or primer extension? Would SF1 be enriched if the U2 snRNA was degraded by RNaseH in the NE?

We did not measure any co-associating RNAs in this experimental approach, but agree that this approach would strengthen the evidence for it.

(6) I'm wondering how additive the effects of QK1 and SF1 are... In Figure 2, if QK1 and SF1 are both knocked down, is the splicing of exon 11 restored to "wt" levels?

This is an interesting question that we were unfortunately unable to address experimentally here.

(7) The first discussion section has two paragraphs that begin "How does competition between SF1..." and "Relatively little is known about how...". I found the discussion and speculation about localization, paraspekles, and lncRNAs interesting but a bit detracting from the strengths of the manuscript. I would suggest shortening these two paragraphs into a single one.

We have revised the Discussion.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors were trying to establish whether competition between the RNA-binding proteins SF1 and QKI controlled splicing outcomes. These two proteins have similar binding sites and protein sequences, but SF1 lacks a dimerization motif and seems to bind a single version of the binding sequence. Importantly, these binding sequences correspond to branchpoint consensus sequences, with SF1 binding leading to productive splicing, but QKI binding leading instead to association with paraspeckle proteins. They show that in human cells SF1 generally activates exons and QKI represses, and a large group of the jointly regulated exons (43% of joint targets) are reciprocally controlled by SF1 and QKI. They focus on one of these exons RAI14 that shows this reciprocal pattern of regulation, and has 2 repeats of the binding site that make it a candidate for joint regulation, and confirm regulation within a minigene context. The authors used the assembly of proteins within nuclear extracts to explain the effect of QKI versus SF1 binding. Finally, the authors show that the expression of QKI is lethal in yeast, and causes splicing defects.

How this fits in the field. This study is interesting and provides a conceptual advance by providing a general rule on how SF1 and QKI interact in relation to binding sites, and the relative molecular fates followed, so is very useful. Most of the analysis seems to focus on one example, although the molecular analysis and global work significantly add to the picture from the previously published paper about NUMB joint regulation by QKI and SF (Zong et al, cited in text as reference 50, that looked at SF1 and QKI binding in relation to a duplicated binding site/branchpoint sequence in NUMB).

Thank you for the encouraging remarks.

Strengths:

The data presented are strong and clear. The ideas discussed in this paper are of wide interest, and present a simple model where two binding sites generate a potentially repressive QKI response, whereas exons that have a single upstream sequence are just regulated by SF1. The assembly of splicing complexes on RNAs derived from RAI14 in nuclear extracts, followed by mass spec gave interesting mechanistic insight into what was occurring as a result of QKI versus SF1 binding.

Weaknesses:

I did not think the title best summarises the take-home message and could be perhaps a bit more modest. Although the authors investigated splicing patterns in yeast and human cells, yeast do not have QKI so there is no ancient competition in that case, and the study did not really investigate physiological or evolutionary outcomes in splicing, although it provides interesting speculation on them. Also as I understood it, the important issue was less conserved branchpoints in higher eukaryotes enabling alternative splicing, rather than competition for the conserved branchpoint sequence. So despite the the data being strong and properly analysed and discussed in the paper, could the authors think whether they fit best with the take-home message provided in the title? Just as a suggestion (I am sure the authors can do a better job), maybe "molecular competition between variant branchpoint sequences predict physiological and evolutionary outcomes in splicing"?

Thank you for this point (Reviewer 2 had a similar comment) and the suggestion. We have revised the title.

Although the authors do provide some global data, most of the detailed analysis is of RAI14. It would have been useful to examine members of the other quadrants in Figure 1C as well for potential binding sites to give a reason why these are not co-regulated in the same way as RAI14. How many of the RAI14 quadrants had single/double sites (the motif analysis seemed to pull out just one), and could one of the non-reciprocally regulated exons be moved into a different quadrant by addition or subtraction of a binding site or changing the branchpoint (using a minigene approach for example).

This is an interesting point that we have considered. Our intent with the focus on RAI14 was to use a naturally occurring intron bps with evidence of strong QKI binding that did not require a high degree of sequence manipulation or engineering.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Most of my recommendations are really centered on the figures. In their current state, they detract from the data shown and could be improved: I recommend the authors use a uniform font. For example, Figure 1E and F have at least three different fonts of varying sizes making it very messy. In Figure 1C, the authors could bold the Ral14 ex11 or simply indicate that the blue is this exon in the legend, thus removing the text from this very busy graph. In Figure 4F, I would recommend, having all the labels the same size and putting those genes of interest like Sf3a1 in bold. This could also be done in Figure 4E.

Thank you for the suggestion and we have edited these (FYI the font in Fig’s 1E and 1F were from the rMAPS default output, but I agree, it gives a sloppy appearance).

(2) In Figures 4D and 4G, is there QKI binding to the downstream deletion mutant after 30 minutes? Also, in Figure 4G, are these all from the same blot? The band sizes seem to be very different between lanes. If these were not on the same blot, the original gels should be submitted.

A small amount of Qki appears to be binding after 30 min. All lanes/blots are from the same gels/membranes; see new Supplemental Figure 4 for the original (uncropped) images of the blots.

(3) The authors should indicate, the source and concentration of the antibodies used for their WB. They should also indicate the primers used for RT-PCRs.

We have revised the methods to include the antibody information and have uploaded a supplemental table 8 with all oligonucleotide sequences used (which I (Sam Fagg) neglected to do initially, so that’s my bad).

Reviewer #2 (Recommendations for the authors):

(1) This may come down to the author's preference but branch point and branch site are frequently two words, not a single compound word (branch point vs. branchpoint). In addition, the authors may want to use branchsite with the abbreviation BS more frequently since they often don't describe the specific point of branching, and bp and bps could be confused for the more frequent abbreviations for base pair(s).

Good suggestion; we have edited the text accordingly.

(2) In general the addition of page numbers and line numbers to the manuscript would greatly aid reviewers!

Point taken…

(3) Introduction; "...under normal growth conditions they are efficiently spliced". I would say MOST introns in yeast are efficiently spliced. This is definitely not universal.

Text edited to indicate that most are efficiently spliced.

(4) Introduction; " recognition of the bps by SF1 (mammals) (20)". The choice of reference 20 is an odd one here. I think the Robin Reed and Michael Rosbash paper was the first to show SF1 was the human homolog of BBP.

Got it, thanks (added #14 here and kept #20 also since it shows the structure of SF1 in complex with a UACUAAC bps.)

(5) Results; "QK1 and SF1 co-regulate.."; it may be useful for the reader if you could explain in more detail why exon inclusion and intron retention are expected outcomes for QK1 knockdown and vice versa for SF1. The exon inclusion here is more obvious than the intron retention phenotype. (In other words, if more exons are included shouldn't it follow that more introns are removed?)

We explain the expected results for exon inclusion in the Introduction and this paragraph of the Results. Although we have observed more intron retention under QKI loss-of-function approaches before, I am uncertain where the reviewer sees that we indicate any expected result for intron retention from either QKI or SF1 knockdown. I believe the statement you refer to might be on line 162 and starts with: “Consistent with potentially opposing functions in splicing…” ?

Also, I agree that if SF1 is a “splicing activator,” one might expect more IR in its absence (but this is not the case; there is, in fact, less), but nonetheless, the opposite outcome is observed with QKI knockdown (more IR). It is unclear why this is the case, and we did not investigate it.

(6) Results; "QK1 and SF1 co-regulate.."; "Thus the most highly represented set.." To me, the most highly represented set is those which are not both QK1-repressed and SF1-activated. Does this indicate that other factors are involved at most sites than simple competition between these two?

We have revised the sentence in question to include the text “by quadrant” in order to convey our meaning more precisely.

(7) Throughout the manuscript, 5 apostrophes and 3 apostrophes are used instead of 5 prime symbols and 3 prime symbols.

Thank you for pointing that out. We have fixed each instance of this.

(8) Sometimes SF1 is written as Sf1. (also Tatsf1)

This was a mouse/human gene/protein nomenclature error that we have fixed; thank you for pointing this out.

(9) You may want to make sure that figures are labeled consistently with the manuscript text. In Figure 1B, it is RI rather than IR. In Figure 4 it is myoblast NE rather than C2C12 nuclear extract.

We have fixed these, checked for other examples, and where relevant, edited those too.

(10) I think Figure 1A could be improved by also including a depiction of the domain arrangements of SF1 and QK1.

Done.

(11) I was a bit confused with all the lines in Figure 1E and 1F. What is the difference between the log (pVal) and upregulated plots? Can these figures be simplified or explained more thoroughly?

Based on this comment and one from Reviewer 1, we have slightly revised the wording (and font) on the output, which hopefully clarifies. These are motif enrichment plots generated by rMAPS (Refs 61 and 62) analysis of rMATS (Ref 60) data for exons more included (depicted by the red lines) or more skipped (depicted by the blue lines) compared to control versus a “background” set of exons that are detectable but unchanged. The -log₁₀ is P-value (dotted line) indicates the significance of exons more included in shRNA treatment vs control shRNA (previously read “upregulated”) compared to background exons that are detectable but unchanged; the solid lines indicate the motif score; these are described in the references indicated.

(12) Figure 1B, it is a bit hard to conclude that there is more AltEx or "RI/IR" in one sample vs. the other from these plots since the points overlay one another. Can you include numbers here?

Added (and deleted Suppl Fig S1, which was simply a chart showing the numbers).

(13) How was PSI calculated in Figure 2A?

VAST-tools (we state this in the legend in the revised version).

You may want to include rel protein (or the lower limit of detection) for Figure 2B to be consistent with 2C. Why is KD of SF1 so poor and variable between 2C and 2D?

We have not investigated this, but these blots show an optimized result that we were able to obtain for the knockdown in each cell type. It may be that HEK293 cells (Fig 2B) have a stronger requirement for SF1 than C2C12 cells…? I would argue that it is not necessarily “poor” in Fig 2C, as we observe ~70% depletion of the protein.

Why are two bands present in the gel?

Two to three isoforms of SF1 are present in most cell types.

A good (or bad, really) example of an SF1 western blot (and knockdown of ~35% in K562 or ~45% in HepG2 can also be seen on the ENCODE project website, for reference:

https://www.encodeproject.org/documents/6001a414-b096-4073-94ff-3af165617eb5/@@download/attachment/SF1_BGKLV28-49.pdf

By comparison, I think ours are much more cosmetically pleasing, and our knockdown (especially in C2C12) is much more efficient.

(14) Figure 3, The asterisk refers to a cryptic product. Can the uaAcuuuCAG be used as a branch point? Presumably the natural 3' SS is now too close so this would result in activation of a downstream 3'SS?

We did not pursue determining the identity of this minor and likely artefactual product, but we (and others) have observed a similar phenomenon when using splicing reporter-based mutational approaches.

(15) For the methods. The "RNA extraction, RT -PCR,..." subheading needs to be on its own line. Please add (w/v) or (v/v) to percentages where appropriate. Please convert ug to the symbol for "micro".

Thank you, we have made these changes.

(16) In Figure 4B, the text here and legend are microscopic. Even with reading glasses, I couldn't make anything out!

We have increased the font sizes for the text and scale bar…when referring to “legend” does the reviewer mean the scale bar?

(17) As a potential discussion item, it is worth noting that SF1 could also repress splicing if it could either not engage with U2AF or be properly displaced by U2 snRNP so the snRNA could pair. I was wondering if QK1 could similarly be activating if it could engage with U2AF. I'm unsure if this could be tested by domain swaps (and is beyond the scope of this paper). It just may be worth speculating about.

Good point and suggestion…we are looking into this.

Reviewer #3 (Recommendations for the authors):

(1) Is the reference in the text to Figure 5F correct for actin splicing (this is just before the discussion)?

I see references several lines up from this, but I do not see a reference just before the discussion…?

(2) I was not sure why the minigene experiments showed such high levels of intron retention that seemed to be impacted also by deletion of the branchpoint sequences, and suggest that the two branchpoints are not equal in strength.

Neither were we, but Reviewer 2 has suggested that degradation of the spliced products could be rapid (NMD substrates) which could complicate the interpretation of what appears to be higher levels of intron retention. Given the possibility that this could be a non-physiological artefact, we have removed the measurement of unspliced reporter and now only show the spliced products (equally subject to degradation) and report their percent inclusion.

Author response:

The following is the authors’ response to the current reviews.

We thank the editors of eLife and the reviewers for their thorough evaluation of our study. As regards the final comments of reviewer 1 please note that all experimental replicates were first analyzed separately, and were then pooled, since the observed changes were comparable between experiments. This mean that statistical analyses were done on pooled biological replicates.

The following is the authors’ response to the original reviews.

General Statements

We thank the reviewers for their thorough and constructive evaluation of our work. We have revised the manuscript carefully and addressed all the criticisms raised, in particular the issues mentioned by several of the reviewers (see point-by-point response below). We have also added a number of explanations in the text for the sake of clarity, while trying to keep the manuscript as concise as possible.

In our view, the novelty of our research is two-fold. From a neurobiological point of view, we provide conclusive evidence for the existence of glycine receptors (GlyRs) at inhibitory synapses in various brain regions including the hippocampus, dentate gyrus and sub-regions of the striatum. This solves several open questions and has fundamental implications for our understanding of the organisation and function of inhibitory synapses in the telencephalon. Secondly, our study makes use of the unique sensitivity of single molecule localisation microscopy (SMLM) to identify low protein copy numbers. This is a new way to think about SMLM as it goes beyond a mere structural characterisation and towards a quantitative assessment of synaptic protein assemblies.

Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity): 

In this manuscript, the authors investigate the nanoscopic distribution of glycine receptor subunits in the hippocampus, dorsal striatum, and ventral striatum of the mouse brain using single-molecule localization microscopy (SMLM). They demonstrate that only a small number of glycine receptors are localized at hippocampal inhibitory synapses. Using dual-color SMLM, they further show that clusters of glycine receptors are predominantly localized within gephyrinpositive synapses. A comparison between the dorsal and ventral striatum reveals that the ventral striatum contains approximately eight times more glycine receptors and this finding is consistent with electrophysiological data on postsynaptic inhibitory currents. Finally, using cultured hippocampal neurons, they examine the differential synaptic localization of glycine receptor subunits (α1, α2, and β). This study is significant as it provides insights into the nanoscopic localization patterns of glycine receptors in brain regions where this protein is expressed at low levels. Additionally, the study demonstrates the different localization patterns of GlyR in distinct striatal regions and its physiological relevance using SMLM and electrophysiological experiments. However, several concerns should be addressed. 

The following are specific comments: 

(1) Colocalization analysis in Figure 1A. The colocalization between Sylite and mEos-GlyRβ appears to be quite low. It is essential to assess whether the observed colocalization is not due to random overlap. The authors should consider quantifying colocalization using statistical methods, such as a pixel shift analysis, to determine whether colocalization frequencies remain similar after artificially displacing one of the channels. 

Following the suggestion of reviewer 1, we re-analysed CA3 images of Glrb^eos/eos hippocampal slices by applying a pixel-shift type of control, in which the Sylite channel (in far red) was horizontally flipped relative to the mEos4b-GlyRβ channel (in green, see Methods). As expected, the number of mEos4b-GlyRβ detections per gephyrin cluster was markedly reduced compared to the original analysis (revised Fig. 1B), confirming that the synaptic mEos4b detections exceed chance levels (see page 5). 

(2) Inconsistency between Figure 3A and 3B. While Figure 3B indicates an ~8-fold difference in the number of mEos4b-GlyRβ detections per synapse between the dorsal and ventral striatum, Figure 3A does not appear to show a pronounced difference in the localization of mEos4bGlyRβ on Sylite puncta between these two regions. If the images presented in Figure 3A are not representative, the authors should consider replacing them with more representative examples or providing an expanded images with multiple representative examples. Alternatively, if this inconsistency can be explained by differences in spot density within clusters, the authors should explain that. 

The pointillist images in Fig. 3A are essentially binary (red-black). Therefore, the density of detections at synapses cannot be easily judged by eye. For clarity, the original images in Fig. 3A have been replaced with two other examples that better reflect the different detection numbers in the dorsal and ventral striatum. 

(3) Quantification in Figure 5. It is recommended that the authors provide quantitative data on cluster formation and colocalization with Sylite puncta in Figure 5 to support their qualitative observations. 

This is an important point that was also raised by the other reviewers. We have performed additional experiments to increase the data volume for analysis. For quantification, we used two approaches. First, we counted the percentage of infected cells in which synaptic localisation of the recombinant receptor subunit was observed (Fig. 5C). We found that mEos4b-GlyRa1 consistently localises at synapses, indicating that all cells express endogenous GlyRb. When neurons were infected with mEos4b-GlyRb, fewer cells had synaptic clusters, meaning that indeed, GlyR alpha subunits are the limiting factor for synaptic targeting. In cultures infected with mEos4b-GlyRa2, only very few neurons displayed synaptic localisation (as judged by epifluorescence imaging). We think this shows that GlyRa2 is less capable of forming heteromeric complexes than GlyRa1, in line with our previous interpretation (see pp. 9-10, 13). 

Secondly, we quantified the total intensity of each subunit at gephyrin-positive domains, both in infected neurons as well as non-infected control cultures (Fig. 5D). We observed that mEos4bGlyRa1 intensity at gephyrin puncta was higher than that of the other subunits, again pointing to efficient synaptic targeting of GlyRa1. Gephyrin cluster intensities (Sylite labelling) were not significantly different in GlyRb and GlyRa2 expressing neurons compared to the uninfected control, indicating that the lentiviral expression of recombinant subunits does not fundamentally alter the size of mixed inhibitory synapses in hippocampal neurons. Interestingly, gephyrin levels were slightly higher in hippocampal neurons expressing mEos4b-GlyRa1. In our view, this comes from an enhanced expression and synaptic targeting of mEos4b-GlyRa1 heteromers with endogenous GlyRb, pointing to a structural role of GlyRa1/b in hippocampal synapses (pp. 10, 13).

The new data and analyses have been described and illustrated in the relevant sections of the manuscript.

(4) Potential for pseudo replication. It's not clear whether they're performing stats tests across biological replica, images, or even synapses. They often quote mean +/- SEM with n = 1000s, and so does that mean they're doing tests on those 1000s? Need to clarify. 

All experiments were repeated at least twice to ensure reproducibility (N independent experiments). Statistical tests were performed on pooled data across the biological replicates; n denotes the number of data points used for testing (e.g., number of synaptic clusters, detections, cells, as specified in each case). We have systematically given these numbers in the revised manuscript (n, N, and other experimental parameters such as the number of animals used, coverslips, images or cells). Data are generally given as mean +/- SEM or as mean +/- SD as indicated.

(5) Does mEoS effect expression levels or function of the protein? Can't see any experiments done to confirm this. Could suggest WB on homogenate, or mass spec? 

The Glrb^eos/eos knock-in mouse line has been characterised previously and does not to display any ultrastructural or functional deficits at inhibitory synapses (Maynard et al. 2021 eLife). GlyRβ expression and glycine-evoked responses were not significantly different to those of the wildtype. The synaptic localisation of mEos4b-GlyRb in KI animals demonstrates correct assembly of heteromeric GlyRs and synaptic targeting. Accordingly, the animals do not display any obvious phenotype. We have clarified this in the manuscript (p. 4). In the case of cultured neurons, long-term expression of fluorescent receptor subunits with lentivirus   has proven ideal to achieve efficient synaptic targeting. The low and continuous supply of recombinant receptors ensures assembly with endogenous subunits to form heteropentameric receptor complexes (e.g. [Patrizio et al. 2017 Sci Rep]). In the present study, lentivirus infection did not induce any obvious differences in the number or size of inhibitory synapses compared to control neurons, as judged by Sylite labelling of synaptic gephyrin puncta (new Fig. 5D).

(6) Quantification of protein numbers is challenging with SMLM. Issues include i) some of FP not correctly folded/mature, and ii) dependence of localisation rate on instrument, excitation/illumination intensities, and also the thresholds used in analysis. Can the authors compare with another protein that has known expression levels- e.g. PSD95? This is quite an ask, but if they could show copy number of something known to compare with, it would be useful. 

We agree that absolute quantification with SMLM is challenging, since the number of detections depends on fluorophore maturation, photophysics, imaging conditions, and analysis thresholds (discussed in Patrizio & Specht 2016, Neurophotonics). For this reason, only very few datasets provide reliable copy numbers, even for well-studied proteins such as PSD-95. One notable exception is the study by Maynard et al. (eLife 2021) that quantified endogenous GlyRβcontaining receptors in spinal cord synapses using SMLM combined with correlative electron microscopy. The strength of this work was the use of a KI mouse strain, which ensures that mEos4b-GlyRβ expression follows intrinsic regional and temporal profiles. The authors reported a stereotypic density of ~2,000 GlyRs/µm² at synapses, corresponding to ~120 receptors per synapse in the dorsal horn and ~240 in the ventral horn, taking into account various parameters including receptor stoichiometry and the functionality of the fluorophore. These values are very close to our own calculations of GlyR numbers at spinal cord synapses that were obtained slightly differently in terms of sample preparation, microscope setup, imaging conditions, and data analysis, lending support to our experimental approach. Nevertheless, the obtained GlyR copy numbers at hippocampal synapses clearly have to be taken as estimates rather than precise figures, because the number of detections from a single mEos4b fluorophore can vary substantially, meaning that the fluorophores are not represented equally in pointillist images. This can affect the copy number calculation for a specific synapse, in particular when the numbers are low (e.g. in hippocampus), however, it should not alter the average number of detections (Fig. 1B) or the (median) molecule numbers of the entire population of synapses (Fig. 1C). We have discussed the limitations of our approach (p. 11).

(7) Rationale for doing nanobody dSTORM not clear at all. They don't explain the reason for doing the dSTORM experiments. Why not just rely on PALM for coincidence measurements, rather than tagging mEoS with a nanobody, and then doing dSTORM with that? Can they explain? Is it to get extra localisations- i.e. multiple per nanobody? If so, localising same FP multiple times wouldn't improve resolution. Also, no controls for nanobody dSTORM experiments- what about non-spec nb, or use on WT sections? 

As discussed above (point 6), the detection of fluorophores with SMLM is influenced by many parameters, not least the noise produced by emitting molecules other than the fluorophore used for labelling. Our study is exceptional in that it attempts to identify extremely low molecule numbers (down to 1). To verify that the detections obtained with PALM correspond to mEos4b, we conducted robust control experiments (including pixel-shift as suggested by the reviewer, see point 1, revised Fig. 1B). The rationale for the nanobody-based dSTORM experiments was twofold: (1) to have an independent readout of the presence of low-copy GlyRs at inhibitory synapses and (2) to analyse the nanoscale organisation of GlyRs relative to the synaptic gephyrin scaffold using dual-colour dSTORM with spectral demixing (see p. 6). The organic fluorophores used in dSTORM (AF647, CF680) ensure high photon counts, essential for reliable co-localisation and distance analysis. PALM and dSTORM cannot be combined in dual-colour mode, as they require different buffers and imaging conditions. 

The specificity of the anti-Eos nanobody was demonstrated by immunohistochemistry in spinal cord cultures expressing mEos4b-GlyRb and wildtype control tissue (Fig. S3). In response to the reviewer's remarks, we also performed a negative control experiment in Glrb^eos/eos slices (dSTORM), in which the nanobody was omitted (new Fig. S4F,G). Under these conditions, spectral demixing produced a single peak corresponding to CF680 (gephyrin) without any AF647 contribution (Fig. S4F). The background detection of "false" AF647 detections at synapses was significantly lower than in the slices labelled with the nanobody. We conclude that the fluorescence signal observed in our dual-colour dSTORM experiments arises from the specific detection of mEos4b-GlyRb by the nanobody, rather than from background, crossreactivity or wrong attribution of colour during spectral demixing. We have added these data and explanations in the results (p. 7) and in the figure legend of Fig. S4F,G.

(8) What resolutions/precisions were obtained in SMLM experiments? Should perform Fourier Ring Correlation (FRC) on SR images to state resolutions obtained (particularly useful for when they're presenting distance histograms, as this will be dependent on resolution). Likewise for precision, what was mean precision? Can they show histograms of localisation precision. 

This is an interesting question in the context of our experiments with low-copy GlyRs, since the spatial resolution of SMLM is limited also by the density of molecules, i.e. the sampling of the structure in question (Nyquist-Shannon criterion). Accordingly, the priority of the PALM experiments was to improve the sensibility of SMLM for the identification of mEos4b-GlyRb subunits, rather than to maximize the spatial resolution. The mean localisation precision in PALM was 33 +/- 12 nm, as calculated from the fitting parameters of each detection (Zeiss, ZEN software), which ultimately result from their signal-to-noise ratio. This is a relatively low precision for SMLM, which can be explained by the low brightness of mEos4b compared to organic fluorophores together with the elevated fluorescence background in tissue slices.

In the case of dSTORM, the aim was to study the relative distribution of GlyRs within the synaptic scaffold, for which a higher localisation precision was required (p. 6). Therefore, detections with a precision ≥ 25 nm were filtered during analysis with NEO software (Abbelight). The retained detections had a mean localisation precision of 12 +/- 5 for CF680 (Sylite) and 11 +/- 4 for AF647 (nanobody). These values are given in the revised manuscript (pp. 18, 22).

(9) Why were DBSCAN parameters selected? How can they rule out multiple localisations per fluor? If low copy numbers (<10), then why bother with DBSCAN? Could just measure distance to each one. 

Multiple detections of the same fluorophore are intrinsic to dSTORM imaging and have not been eliminated from the analysis. Small clusters of detections likely represent individual molecules (e.g. single receptors in the extrasynaptic regions, Fig. 2A). DBSCAN is a robust clustering method that is quite insensitive to minor changes in the choice of parameters. For dSTORM of synaptic gephyrin clusters (CF680), a relatively low length (80 nm radius) together with a high number of detections (≥ 50 neighbours) were chosen to reconstruct the postsynaptic domain with high spatial resolution (see point 8). In the case of the GlyR (nanobody-AF647), the clustering was done mostly for practical reasons, as it provided the coordinates of the centre of mass of the detections. The low stringency of this clustering (200 nm radius, ≥ 5 neighbours) effectively filters single detections that can result from background noise or incorrect demixing. An additional reference explaining the use of DBSCAN including the choice of parameters is given on p. 22 (see also R2 point 4).

(10) For microscopy experiment methods, state power densities, not % or "nominal power". 

Done. We now report the irradiance (laser power density) instead of nominal power (pp. 18, 21). 

(11) In general, not much data presented. Any SI file with extra images etc.? 

The original submission included four supplementary figures with additional data and representative images that should have been available to the reviewer (Figs. S1-S4). The SI file has been updated during revision (new Fig. S4E-G). 

(12) Clarification of the discussion on GlyR expression and synaptic localization: The discussion on GlyR expression, complex formation, and synaptic localization is sometimes unclear, and needs terminological distinctions between "expression level", "complex formation" and "synaptic localization". For example, the authors state:"What then is the reason for the low protein expression of GlyRβ? One possibility is that the assembly of mature heteropentameric GlyR complexes depends critically on the expression of endogenous GlyR α subunits." Does this mean that GlyRβ proteins that fail to form complexes with GlyRα subunits are unstable and subject to rapid degradation? If so, the authors should clarify this point. The statement "This raises the interesting possibility that synaptic GlyRs may depend specifically on the concomitant expression of both α1 and β transcripts." suggests a dependency on α1 and β transcripts. However, is the authors' focus on synaptic localization or overall protein expression levels? If this means synaptic localization, it would be beneficial to state this explicitly to avoid confusion. To improve clarity, the authors should carefully distinguish between these different aspects of GlyR biology throughout the discussion. Additionally, a schematic diagram illustrating these processes would be highly beneficial for readers. 

We thank the reviewer to point this out. We are dealing with several processes; protein expression that determines subunit availability and the assembly of pentameric GlyRs complexes, surface expression, membrane diffusion and accumulation of GlyRb-containing receptor complexes at inhibitory synapses. We have edited the manuscript, particularly the discussion and tried to be as clear as possible in our wording.

We chose not to add a schematic illustration for the time being, because any graphical representation is necessarily a simplification. Instead, we preferred to summarise the main numbers in tabular form (Table 1). We are of course open to any other suggestions.

(13) Interpretation of GlyR localization in the context of nanodomains. The distribution of GlyR molecules on inhibitory synapses appears to be non-homogeneous, instead forming nanoclusters or nanodomains, similar to many other synaptic proteins. It is important to interpret GlyR localization in the context of nanodomain organization. 

The dSTORM images in Fig. 2 are pointillist representations that show individual detections rather than molecules. Small clusters of detections are likely to originate from a single AF647 fluorophore (in the case of nanobody labelling) and therefore represent single GlyRb subunits. Since GlyR copy numbers are so low at hippocampal synapses (≤ 5), the notion of nanodomain is not directly applicable. Our analysis therefore focused on the integration of GlyRs within the postsynaptic scaffold, rather than attempting to define nanodomain structures (see also response to point 8 of R1). A clarification has been added in the revised manuscript (p. 6).

Reviewer #1 (Significance): 

The paper presents biological and technical advances. The biological insights revolve mostly on the documentation of Glycine receptors in particular synapses in forebrain, where they are typically expressed at very low levels. The authors provide compelling data indicating that the expression is of physiological significance. The authors have done a nice job of combining genetically-tagged mice with advanced microscopy methods to tackle the question of distributions of synaptic proteins. Overall these advances are more incremental than groundbreaking. 

We thank the reviewer for acknowledging both the technical and biological advances of our study. While we recognize that our work builds upon established models, we consider that it also addresses important unresolved questions, namely that GlyRs are present and specifically anchored at inhibitory synapses in telencephalic regions, such as the hippocampus and striatum. From a methodological point of view, our study demonstrates that SMLM can be applied not only for structural analysis of highly abundant proteins, but also to reliably detect proteins present at very low copy numbers. This ability to identify and quantify sparse molecule populations adds a new dimension to SMLM applications, which we believe increases the overall impact of our study beyond the field of synaptic neuroscience.

Reviewer #2 (Evidence, reproducibility and clarity): 

In their manuscript "Single molecule counting detects low-copy glycine receptors in hippocampal and striatal synapses" Camuso and colleagues apply single molecule localization microscopy (SMLM) methods to visualize low copy numbers of GlyRs at inhibitory synapses in the hippocampal formation and the striatum. SMLM analysis revealed higher copy numbers in striatum compared to hippocampal inhibitory synapses. They further provide evidence that these low copy numbers are tightly linked to post-synaptic scaffolding protein gephyrin at inhibitory synapses. Their approach profits from the high sensitivity and resolution of SMLM and challenges the controversial view on the presence of GlyRs in these formations although there are reports (electrophysiology) on the presence of GlyRs in these particular brain regions. These new datasets in the current manuscript may certainly assist in understanding the complexity of fundamental building blocks of inhibitory synapses. 

However I have some minor points that the authors may address for clarification: 

(1) In Figure 1 the authors apply PALM imaging of mEos4b-GlyRß (knockin) and here the corresponding Sylite label seems to be recorded in widefield, it is not clearly stated in the figure legend if it is widefield or super-resolved. In Fig 1 A - is the scale bar 5 µm? Some Sylite spots appear to be sized around 1 µm, especially the brighter spots, but maybe this is due to the lower resolution of widefield imaging? Regarding the statistical comparison: what method was chosen to test for normality distribution, I think this point is missing in the methods section. 

This is correct; the apparent size of the Sylite spots does not reflect the real size of the synaptic gephyrin domain due to the limited resolution of widefield imaging including the detection of outof-focus light. We have clarified in the legend of Fig. 1A that Sylite labelling was with classic epifluorescence microscopy. The scale bar in Fig. 1A corresponds to 5 µm. Since the data were not normally distributed, nonparametric tests (Kruskal- Wallis one-way ANOVA with Dunn’s multiple comparison test or Mann-Whitney U-test for pairwise comparisons) were used (p. 23). 

Moreover I would appreciate a clarification and/or citation that the knockin model results in no structural and physiological changes at inhibitory synapses, I believe this model has been applied in previous studies and corresponding clarification can be provided. 

The Glrbeos/eos mouse model has been described previously and does not exhibit any structural or physiological phenotypes (Maynard et al. 2021 eLife). The issue was also raised by reviewer R1 (point 5) and has been clarified in the revised manuscript (p. 4).

(2) In the next set of experiments the authors switch to demixing dSTORM experiments - an explanation why this is performed is missing in the text - I guess better resolution to perform more detailed distance measurements? For these experiments: which region of the hippocampus did the authors select, I cannot find this information in legend or main text. 

Yes, the dSTORM experiments enable dual-colour structural analysis at high spatial resolution (see response to R1 point 7). An explanation has been added (p. 6).

(3) Regarding parameters of demixing experiments: the number of frames (10.000) seems quite low and the exposure time higher than expected for Alexa 647. Can the authors explain the reason for chosing these particular parameters (low expression profile of the target - so better separation?, less fluorophores on label and shorter collection time?) or is there a reference that can be cited? The laser power is given in the methods in percentage of maximal output power, but for better comparison and reproducibility I recommend to provide the values of a power meter (kW/cm2) as lasers may change their maximum output power during their lifetime. 

Acquisition parameters (laser power, exposure time) for dSTORM were chosen to obtain a good localisation precision (~12 nm; see R1 point 8). The number of frames is adequate to obtain well sampled gephyrin scaffolds in the CF680 channel. In the case of the GlyR (nanobody-AF647), the concept of spatial resolution does not really apply due to the low number of targets (see R1, point 13). Power density (irradiance) values have now been given (pp. 18, 21).

(4) For analysis of subsynaptic distribution: how did the authors decide to choose the parameters in the NEO software for DBSCAN clustering - was a series of parameters tested to find optimal conditions and did the analysis start with an initial test if data is indeed clustered (K-ripley) or is there a reference in literature that can be provided? 

DBSCAN parameters were optimised manually, by testing different values. Identification of dense and well-delimited gephyrin clusters (CF680) was achieved with a small radius and a high number of detections (80 nm, ≥ 50 neighbours), whereas filtering of low-density background in the AF647 channel (GlyRs) required less stringent parameters (200 nm, ≥ 5) due to the low number of target molecules. Similar parameters were used in a previous publication (Khayenko et al. 2022, Angewandte Chemie). The reference has been provided on p. 22 (see also R1 point 9).

(5) A conclusion/discussion of the results presented in Figure 5 is missing in the text/discussion. 

This part of the manuscript has been completely overhauled. It includes new experimental data, quantification of the data (new Fig.5), as well as the discussion and interpretation of our findings (see also R1, point 3). In agreement with our earlier interpretation, the data confirm that low availability of GlyRa1 subunits limits the expression and synaptic targeting of GlyRa1/b heteropentamers. The observation that GlyRa1 overexpression with lentivirus increases the size of the postsynaptic gephyrin domain further points to a structural role, whereby GlyRs can enhance the stability (and size) of inhibitory synapses in hippocampal neurons, even at low copy numbers (pp. 13-14). 

(6) In line 552 "suspension" is misleading, better use "solution" 

Done.

Reviewer #2 (Significance): 

Significance: The manuscript provides new insights to presence of low-copy numbers by visualizing them via SMLM. This is the first report that visualizes GlyR optically in the brain applying the knock-in model of mEOS4b tagged GlyRß and quantifies their copy number comparing distribution and amount of GlyRs from hippocampus and striatum. Imaging data correspond well to electrophysiological measurements in the manuscript. 

Field of expertise: Super-Resolution Imaging and corresponding analysis 

Reviewer #4 (Evidence, reproducibility and clarity): 

In this study, Camuso et al., make use of a knock-in mouse model expressing endogenously mEos4b-tagged GlyRβ to detect endogenous glycine receptors using single-molecule localization microscopy. The main conclusion from this study is that in the hippocampus GlyRβ molecules are barely detected, while inhibitory synapses in the ventral striatum seem to express functionally relevant GlyR numbers. 

I have a few points that I hope help to improve the strength of this study. 

- In the hippocampus, this study finds that the numbers of detections are very low. The authors perform adequate controls to indicate that these localizations are above noise level. Nevertheless, it remains questionable that these reflect proper GlyRs. The suggestion that in hippocampal synapses the low numbers of GlyRβ molecules "are important in assembly or maintenance of inhibitory synaptic structures in the brain" is on itself interesting, but is not at all supported. It is also difficult to envision how such low numbers could support the structure of a synapse. A functional experiment showing that knockdown of GlyRs affects inhibitory synapse structure in hippocampal neurons would be a minimal test of this. 

It is not clear what the reviewer means by “it remains questionable that these reflect proper GlyRs”. The PALM experiments include a series of stringent controls (see R1, point 1) demonstrating the existence of low-copy GlyRs at inhibitory synapses in the hippocampus (Fig. 1) and in the striatum (Fig. 3), and are backed up by dSTORM experiments (Fig. 2). We have no reason to doubt that these receptors are fully functional (as demonstrated for the ventral striatum (Fig. 4). However, due to their low number, a role in inhibitory synaptic transmission is clearly limited, at least in the hippocampus and dorsal striatum. 

We therefore propose a structural role, where the GlyRs could be required to stabilise the postsynaptic gephyrin domain in hippocampal neurons. This is based on the idea that the GlyRgephyrin affinity is much higher than that of the GABAAR-gephyrin interaction (reviewed in Kasaragod & Schindelin 2018 Front Mol Neurosci). Accordingly, there is a close relationship between GlyRs and gephyrin numbers, sub-synaptic distribution, and dynamics in spinal cord synapses that are mostly glycinergic (Specht et al. 2013 Neuron; Maynard et al. 2021 eLife; Chapdelaine et al. 2021 Biophys J). It is reasonable to assume that low-copy GlyRs could play a similar structural role at hippocampal synapses. A knockdown experiment targeting these few receptors is technically very challenging and beyond the scope of this study. However, in response to the reviewer's question we have conducted new experiments in cultured hippocampal neurons (new Fig. 5). They demonstrate that overexpression of GlyRa1/b heteropentamers increases the size of the postsynaptic domain in these neurons, supporting our interpretation of a structural role of low-copy GlyRs (p. 14).

- The endogenous tagging strategy is a very strong aspect of this study and provides confidence in the labeling of GlyRβ molecules. One caveat however, is that this labeling strategy does not discriminate whether GlyRβ molecules are on the cell membrane or in internal compartments. Can the authors provide an estimate of the ratio of surface to internal GlyRβ molecules? 

Gephyrin is known to form a two-dimensional scaffold below the synaptic membrane to which inhibitory GlyRs and GABAARs attach (reviewed in Alvarez 2017 Brain Res). The majority of the synaptic receptors are therefore thought to be located in the synaptic membrane, which is supported by the close relationship between the sub-synaptic distribution of GlyRs and gephyrin in spinal cord neurons (e.g. Maynard et al. 2021 eLife). To demonstrate the surface expression of GlyRs at hippocampal synapses we labelled cultured hippocampal neurons expressing mEos4b-GlyRa1 with anti-Eos nanobody in non-permeabilised neurons (see Author response image 1). The close correspondence between the nanobody (AF647) and the mEos4b signal confirms that the majority of the GlyRs are indeed located in the synaptic membrane.

Author response image 1.

Left: Lentivirus expression of mEos4b-GlyRa1 in fixed and non-permeabilised hippocampal neurons (mEos4b signal). Right: Surface labelling of the recombinant subunit with anti-Eos nanoboby (AF647). 

- “We also estimated the absolute number of GlyRs per synapse in the hippocampus. The number of mEos4b detections was converted into copy numbers by dividing the detections at synapses by the average number of detections of individual mEos4b-GlyRβ containing receptor complexes”. In essence this is a correct method to estimate copy numbers, and the authors discuss some of the pitfalls associated with this approach (i.e., maturation of fluorophore and detection limit). Nevertheless, the authors did not subtract the number of background localizations determined in the two negative control groups. This is critical, particularly at these low-number estimations. 

We fully agree that background subtraction can be useful with low detection numbers. In the revised manuscript, copy numbers are now reported as background-corrected values. Specifically, the mean number of detections measured in wildtype slices was used to calculate an equivalent receptor number, which was then subtracted from the copy number estimates across hippocampus, spinal cord and striatum. This procedure is described in the methods (p. 20) and results (p. 5, 8), and mentioned in the figure legends of Fig. 1C, 3C. The background corrected values are given in the text and Table 1.

- Furthermore, the authors state that "The advantage of this estimation is that it is independent of the stoichiometry of heteropentameric GlyRs". However, if the stoichometry is unknown, the number of counted GlyRβ subunits cannot simply be reported as the number of GlyRs. This should be discussed in more detail, and more carefully reported throughout the manuscript. 

The reviewer is right to point this out. There is still some debate about the stoichiometry of heteropentameric GlyRs. Configurations with 2a:3b, 3a:2b and 4a:1b subunits have been advanced (e.g. Grudzinska et al. 2005 Neuron; Durisic et al. 2012 J Neurosci; Patrizio et al. 2017 Sci Rep; Zhu & Gouaux 2021 Nature). We have therefore chosen a quantification that is independent of the underlying stoichiometry. Since our quantification is based on very sparse clusters of mEos4b detections that likely originate from a single receptor complex (irrespective of its stoichiometry), the reported values actually reflect the number of GlyRs (and not GlyRb subunits). We have clarified this in the results (p. 5) and throughout the manuscript (Table 1). 

- The dual-color imaging provides insights in the subsynaptic distribution of GlyRβ molecules in hippocampal synapses. Why are similar studies not performed on synapses in the ventral striatum where functionally relevant numbers of GlyRβ molecules are found? Here insights in the subsynaptic receptor distribution would be of much more interest as it can be tight to the function. 

This is an interesting suggestion. However, the primary aim of our study was to identify the existence of GlyRs in hippocampal regions. At low copy numbers, the concept of sub-synaptic domains (SSDs, e.g. Yang et al. 2021 EMBO Rep) becomes irrelevant (see R1 point 13). It should be pointed out that the dSTORM pointillist images (Fig. 2A) represent individual GlyR detections rather than clusters of molecules. In the striatum, our specific purpose was to solve an open question about the presence of GlyRs in different subregions (putamen, nucleus accumbens).

- It is unclear how the experiments in Figure 5 add to this study. These results are valid, but do not seem to directly test the hypothesis that "the expression of α subunits may be limiting factor controlling the number of synaptic GlyRs". These experiments simply test if overexpressed α subunits can be detected. If the α subunits are limiting, measuring the effect of α subunit overexpression on GlyRβ surface expression would be a more direct test. 

Both R1 and R2 have also commented on the data in Fig. 5 and their interpretation. We have substantially revised this section as described before (see R1 point 3) including additional experiments and quantification of the data (new Fig. 5). The findings lend support to our earlier hypothesis that GlyR alpha subunits (in particular GlyRa1) are the limiting factor for the expression of heteropentameric GlyRa/b in hippocampal neurons (pp. 13-14). Since the GlyRa1 subunit itself does not bind to gephyrin (Patrizio et al. 2017 Sci Rep), the synaptic localisation of the recombinant mEos4b-GlyRa1 subunits is proof that they have formed heteropentamers with endogenous GlyRb subunits and driven their membrane trafficking, which the GlyRb subunits are incapable of doing on their own.

Reviewer #4 (Significance): 

These results are based on carefully performed single-molecule localization experiments, and are well-presented and described. The knockin mouse with endogenously tagged GlyRβ molecules is a very strong aspect of this study and provides confidence in the labeling, the combination with single-molecule localization microscopy is very strong as it provides high sensitivity and spatial resolution. 

The conceptual innovation however seems relatively modest, these results confirm previous studies but do not seem to add novel insights. This study is entirely descriptive and does not bring new mechanistic insights. 

This study could be of interest to a specialized audience interested in glycine receptor biology, inhibitory synapse biology and super-resolution microscopy. 

My expertise is in super-resolution microscopy, synaptic transmission and plasticity 

As we have stated before, the novelty of our study lies in the use of SMLM for the identification of very small numbers of molecules, which requires careful control experiments. This is something that has not been done before and that can be of interest to a wider readership, as it opens up SMLM for ultrasensitive detection of rare molecular events. Using this approach, we solve two open scientific questions: (1) the demonstration that low-copy GlyRs are present at inhibitory synapses in the hippocampus, (2) the sub-region specific expression and functional role of GlyRs in the ventral versus dorsal striatum.

The following review was provided later under the name “Reviewer #4”. To avoid confusion with the last reviewer from above we will refer to this review as R4-2.

Reviewer #4-2 (Evidence, reproducibility and clarity):  

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors investigate the presence of synaptic glycine receptors in the telencephalon, whose presence and function is poorly understood. 

Using a transgenically labeled glycine receptor beta subunit (Glrb-mEos4b) mouse model together with super-resolution microscopy (SLMM, dSTORM), they demonstrate the presence of a low but detectable amount of synaptically localized GLRB in the hippocampus. While they do not perform a functional analysis of these receptors, they do demonstrate that these subunits are integrated into the inhibitory postsynaptic density (iPSD) as labeled by the scaffold protein gephyrin. These findings demonstrate that a low level of synaptically localized glycerine receptor subunits exist in the hippocampal formation, although whether or not they have a functional relevance remains unknown.

They then proceed to quantify synaptic glycine receptors in the striatum, demonstrating that the ventral striatum has a significantly higher amount of GLRB co-localized with gephyrin than the dorsal striatum or the hippocampus. They then recorded pharmacologically isolated glycinergic miniature inhibitory postsynaptic currents (mIPSCs) from striatal neurons. In line with their structural observations, these recordings confirmed the presence of synaptic glycinergic signaling in the ventral striatum, and an almost complete absence in the dorsal striatum. Together, these findings demonstrate that synaptic glycine receptors in the ventral striatum are present and functional, while an important contribution to dorsal striatal activity is less likely.

Lastly, the authors use existing mRNA and protein datasets to show that the expression level of GLRA1 across the brain positively correlates with the presence of synaptic GLRB.

The authors use lentiviral expression of mEos4b-tagged glycine receptor alpha1, alpha2, and beta subunits (GLRA1, GLRA1, GLRB) in cultured hippocampal neurons to investigate the ability of these subunits to cause the synaptic localization of glycine receptors. They suggest that the alpha1 subunit has a higher propensity to localize at the inhibitory postsynapse (labeled via gephyrin) than the alpha2 or beta subunits, and may therefore contribute to the distribution of functional synaptic glycine receptors across the brain.

Major comments:

- Are the key conclusions convincing?

The authors are generally precise in the formulation of their conclusions.

(1) They demonstrate a very low, but detectable, amount of a synaptically localized glycine receptor subunit in a transgenic (GlrB-mEos4b) mouse model. They demonstrate that the GLRB-mEos4b fusion protein is integrated into the iPSD as determined by gephyrin labelling. The authors do not perform functional tests of these receptors and do not state any such conclusions.

(2) The authors show that GLRB-mEos4b is clearly detectable in the striatum and integrated into gephyrin clusters at a significantly higher rate in the ventral striatum compared to the dorsal striatum, which is in line with previous studies.

(3) Adding to their quantification of GLRB-mEos4b in the striatum, the authors demonstrate the presence of glycinergic miniature IPSCs in the ventral striatum, and an almost complete absence of mIPSCs in the dorsal striatum. These currents support the observation that GLRB-mEos4b is more synaptically integrated in the ventral striatum compared to the dorsal striatum.

(4) The authors show that lentiviral expression of GLRA1-mEos4b leads to a visually higher number of GLR clusters in cultured hippocampal neurons, and a co-localization of some clusters with gephyrin. The authors claim that this supports the idea that GLRA1 may be an important driver of synaptic glycine receptor localization. However, no quantification or statistical analysis of the number of puncta or their colocalization with gephyrin is provided for any of the expressed subunits. Such a claim should be supported by quantification and statistics 

A thorough analysis and quantification of the data in Fig.5 has been carried out as requested by all the other reviewers (e.g. R1, point 3). The new data and results have been described in the revised manuscript (pp. 9-10, 13-14).

- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

One unaddressed caveat is the fact that a GLRB-mEos4b fusion protein may behave differently in terms of localization and synaptic integration than wild-type GLRB. While unlikely, it is possible that mEos4b interacts either with itself or synaptic proteins in a way that changes the fused GLRB subunit’s localization. Such an effect would be unlikely to affect synaptic function in a measurable way, but might be detected at a structural level by highly sensitive methods such as SMLM and STORM in regions with very low molecule numbers (such as the hippocampus). Since reliable antibodies against GLRB in brain tissue sections are not available, this would be difficult to test. Considering that no functional measures of the hippocampal detections exist, we would suggest that this possible caveat be mentioned for this particular experiment.

This question has also been raised before (R1, point 5). According to an earlier study the mEos4b-GlyRb knock-in does not cause any obvious phenotypes, with the possible exception of minor loss of glycine potency (Maynard et al. 2021 eLife). The fact that the synaptic levels in the spinal cord in heterozygous animals are precisely half of those of homozygous animals argues against differences in receptor expression, heteropentameric assembly, forward trafficking to the plasma membrane and integration into the synaptic membrane as confirmed using quantitative super-resolution CLEM (Maynard et al. 2021 eLife). Accordingly, we did not observe any behavioural deficits in these animals, making it a powerful experimental model. We have added this information in the revised manuscript (p. 4). 

In addition, without any quantification or statistical analysis, the author’s claims regarding the necessity of GLRA1 expression for the synaptic localization of glycine receptors in cultured hippocampal neurons should probably be described as preliminary (Fig. 5).

As mentioned before, we have substantially revised this part (R1, point 3). The quantification and analysis in the new Fig. 5 support our earlier interpretation.

- Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation.

The authors show that there is colocalization of gephyrin with the mEos4b-GlyRβ subunit using the Dual-colour SMLM. This is a powerful approach that allows for a claim to be made on the synaptic location of the glycine receptors. The images presented in Figure 1, together with the distance analysis in Figure 2, display the co-localization of the fluorophores. The co-localization images in all the selected regions, hippocampus and striatum, also show detections outside of the gephyrin clusters, which the authors refer to as extrasynaptic. These punctated small clusters seem to have the same size as the ones detected and assigned as part of the synapse. It would be informative if the authors analysed the distribution, density and size of these nonsynaptic clusters and presented the data in the manuscript and also compared it against the synaptic ones. Validating this extrasynaptic signal by staining for a dendritic marker, such as MAP-2 or maybe a somatic marker and assessing the co-localization with the non-synaptic clusters would also add even more credibility to them being extrasynaptic. 

The existence of extrasynaptic GlyRs is well attested in spinal cord neurons (e.g. Specht et al. 2013 Neuron; this study see Fig. S2). The fact that these appear as small clusters of detections in SMLM recordings results from the fact that a single fluorophore can be detected several times in consecutive image frames and because of blinking. Therefore, small clusters of detections likely represent single GlyRs (that can be counted), and not assemblies of several receptor complexes. Due to their diffusion in the neuronal membrane, they are seen as diffuse signals throughout the somatodendritic compartment in epifluorescence images (e.g. Fig. 5A). SMLM recordings of the same cells resolves this diffuse signal into discrete nanoclusters representing individual receptors (Fig. 5B). It is not clear what information co-localisation experiments with specific markers could provide, especially in hippocampal neurons, in which the copy numbers (and density) of GlyRs is next to zero.

In addition we would encourage the authors to quantify the clustering and co-localization of virally expressed GLRA1, GLRA2, and GLRB with gephyrin in order to support the associated claims (Fig. 5). Preferably, the density of GLR and gephyrin clusters (at least on the somatic surface, the proximal dendrites, or both) as well as their co-localization probability should be quantified if a causal claim about subunit-specific requirements for synaptic localization is to be made.

Quantification of the data have been carried out (new Fig.5C,D). The results have been described before (R1, point 3) and support our earlier interpretation of the data (pp. 13-14).

Lastly, even though it may be outside of the scope of such a study analysing other parts of the hippocampal area could provide additional important information. If one looks at the Allen Institute’s ISH of the beta subunit the strongest signal comes from the stratum oriens in the CA1 for example, suggesting that interneurons residing there would more likely have a higher expression of the glycine receptors. This could also be assessed by looking more carefully at the single cell transcriptomics, to see which cell types in the hippocampus show the highest mRNA levels. If the authors think that this is too much additional work, then perhaps a mention of this in the discussion would be good. 

We have added the requested information from the ISH database of the Allen Institute in the discussion as suggested by the reviewer (p. 12). However, in combination with the transcriptomic data (Fig. S1) our finding strongly suggest that the expression of synaptic GlyRs depends on the availability of alpha subunits rather than on the presence of the GlyRb transcript. This is obvious when one compares the mRNA levels in the hippocampus with those in the basal ganglia (striatum) and medulla. While the transcript concentrations of GlyRb are elevated in all three regions and essentially the same, our data show that the GlyRb copy numbers at synapses differ over more than 2 orders of magnitude (Fig. 1B, Table 1). 

- 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.

Since the labeling and some imaging has been performed already, the requested experiment would be a matter of deploying a method of quantification. In principle, it should not require any additional wet-lab experiments, although it may require additional imaging of existing samples.

- Are the data and the methods presented in such a way that they can be reproduced?

Yes, for the most part.

- Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

- Specific experimental issues that are easily addressable.

N/A

- Are prior studies referenced appropriately?

Yes

- Are the text and figures clear and accurate?

Yes, although quantification in figure 5 is currently not present.

A quantification has been added (see R1, point 3).

- Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This paper presents a method that could be used to localize receptors and perhaps other proteins that are in low abundance or for which a detailed quantification is necessary. I would therefore suggest that Figure S4 is included into Figure 2 as the first panel, showcasing the demixing, followed by the results. 

We agree in principle with this suggestion. However, the revised Fig. S4 is more complex and we think that it would distract from the data shown in Fig. 2. Given that Fig. S4 is mostly methodological and not essential to understand the text, we have kept it in the supplement for the time being. We leave the final decision on this point to the editor.

Reviewer #4-2 (Significance): 

[This review was supplied later]

- Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Using a novel and high resolution method, the authors have provided strong evidence for the presence of glycine receptors in the murine hippocampus and in the dorsal striatum. The number of receptors calculated is small compared to the numbers found in the ventral striatum. This is the first study to quantify receptor numbers in these region. In addition it also lays a roadmap for future studies addressing similar questions. 

- Place the work in the context of the existing literature (provide references, where appropriate).

This is done well by the authors in the curation of the literature. As stated above, the authors have filled a gap in the presence of glycine receptors in different brain regions, a subject of importance in understanding the role they play in brain activity and function. 

- State what audience might be interested in and influenced by the reported findings.

Neuroscientists working at the synaptic level, on inhibitory neurotransmission and on fundamental mechanisms of expression of genes at low levels and their relationship to the presence of the protein would be interested. Furthermore, researchers in neuroscience and cell biology may benefit from and be inspired by the approach used in this manuscript, to potentially apply it to address their own aims. 

We thank the reviewer for the positive assessment of the technical and biological implications of our work, as well as the interest of our findings to a wide readership of neuroscientists and cell biologists. 

- Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Synaptic transmission, inhibitory cells and GABAergic synapses functionally and structurally, cortex and cortical circuits. No strong expertise in super-resolution imaging methods.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review): 

Summary: 

This very thorough anatomical study addresses the innervation of the Drosophila male reproductive tract. Two distinct glutamatergic neuron types were classified: serotonergic (SGNs) and octopaminergic (OGNs). By expansion microscopy, it was established that glutamate and serotonin /octopamine are co-released. The expression of different receptors for 5-HT and OA in muscles and epithelial cells of the innervation target organs was characterized. The pattern of neurotransmitter receptor expression in the target organs suggests that seminal fluid and sperm transport and emission are subjected to complex regulation. While silencing of abdominal SGNs leads to male infertility and prevents sperm from entering the ejaculatory duct, silencing of OGNs does not render males infertile. 

Strengths: 

The studied neurons were analysed with different transgenes and methods, as well as antibodies against neurotransmitter synthesis enzymes, building a consistent picture of their neurotransmitter identity. The careful anatomical description of innervation patterns together with receptor expression patterns of the target organs provides a solid basis for advancing the understanding of how seminal fluid and sperm transport and emission are subjected to complex regulation. The functional data showing that SGNs are required for male fertility and for the release of sperm from the seminal vesicle into the ejaculatory duct is convincing. 

Weaknesses: 

The functional analysis of the characterized neurons is not as comprehensive as the anatomical description, and phenotypic characterization was limited to simple fertility assays. It is understandable that a full functional dissection is beyond the scope of the present work. The paper contains experiments showing neuron-independent peristaltic waves in the reproductive tract muscles, which are thematically not very well integrated into the paper. Although very interesting, one wonders if these experiments would not fit better into a future work that also explores these peristaltic waves and their interrelation with neuromodulation mechanistically. 

Reviewer #2 (Public review): 

Summary: 

Cheverra et al. present a comprehensive anatomical and functional analysis of the motor neurons innervating the male reproductive tract in Drosophila melanogaster, addressing a gap in our understanding of the peripheral circuits underlying ejaculation and male fertility. They identify two classes of multi-transmitter motor neurons-OGNs (octopamine/glutamate) and SGNs (serotonin/glutamate)-with distinct innervation patterns across reproductive organs. The authors further characterize the differential expression of glutamate, octopamine, and serotonin receptors in both epithelial and muscular tissues of these organs. Behavioral assays reveal that SGNs are essential for male fertility, whereas OGNs and glutamatergic transmission are dispensable. This work provides a high-resolution map linking neuromodulatory identity to organ-specific motor control, offering a valuable framework to explore the neural basis of male reproductive function. 

Strengths: 

Through the use of an extensive set of GAL4 drivers and antibodies, this work successfully and precisely defines the neurons that innervate the male reproductive tract, identifying the specific organs they target and the nature of the neurotransmitters they release. It also characterizes the expression patterns and localization of the corresponding neurotransmitter receptors across different tissues. The authors describe two distinct groups of dual-identity neurons innervating the male reproductive tract: OGNs, which co-express octopamine and glutamate, and SGNs, which co-express serotonin and glutamate. They further demonstrate that the various organs within the male reproductive system differentially express receptors for these neurotransmitters. Based on these findings, the authors propose that a single neuron capable of co-releasing a fast-acting neurotransmitter alongside a slower-acting one may more effectively synchronize and stagger events that require precise timing. This, together with the differential expression of ionotropic glutamate receptors and metabotropic aminergic receptors in postsynaptic muscle tissue, adds an additional layer of complexity to the coordinated regulation of fluid secretion, organ contractility, and directional sperm movement-all contributing to the optimization of male fertility. 

Weaknesses: 

The main weakness of the manuscript is the lack of detail in the presentation of the results. Specifically, all microscopy image figures are missing information about the number of samples (N), and in the case of colocalization experiments, quantitative analyses are not provided. Additionally, in the first behavioral section, it would be beneficial to complement the data table with figures similar to those presented later in the manuscript for consistency and clarity. 

Wider context: 

This study delivers the first detailed anatomical map connecting multi-transmitter motor neurons with specific male reproductive structures. It highlights a previously unrecognized functional specialization between serotonergic and octopaminergic pathways and lays the groundwork for exploring fundamental neural mechanisms that regulate ejaculation and fertility in males. The principles uncovered here may help explain how males of Drosophila and other organisms adjust reproductive behaviors in response to environmental changes. Furthermore, by shedding light on how multi-transmitter systems operate in reproductive control, this model could provide insights into therapeutic targets for conditions such as male infertility and prostate cancer, where similar neuronal populations are involved in humans. Ultimately, this genetically accessible system serves as a powerful tool for uncovering how multi-transmitter neurons orchestrate coordinated physiological actions necessary for the functioning of complex organs. 

Reviewer #3 (Public review): 

Summary: 

This work provides an overview of the motor neuron landscape in the male reproductive system. Some work had been done to elucidate the circuits of ejaculation in the spine, as well as the cord, but this work fills a gap in knowledge at the level of the reproductive organs. Using complementary approaches, the authors show that there are two types of motor neurons that are mutually exclusive: neurons that co-express octopamine and glutamate and neurons that co-express serotonin and glutamate. They also show evidence that both types of neurons express large dense core vesicles, indicating that neuropeptides play a role in male fertility. This paper provides a thorough characterization of the expression of the different glutamate, octopamine, and serotonin receptors in the different organs and tissues of the male reproductive system. The differential expression in different tissues and organs allows building initial theories on the control of emission and expulsion. Additionally, the authors characterize the expression of synaptic proteins and the neuromuscular junction sites. On a mechanistic level, the authors show that neither octopamine/glutamate neuron transmission nor glutamate transmission in serotonin/glutamate neurons is required for male fertility. This final result is quite surprising and opens up many questions on how ejaculation is coordinated. 

Strengths: 

This work fills an important gap in the characterization of innervation of the male reproductive system by providing an extensive characterization of the motor neurons and the potential receptors of motor neuron release. The authors show convincing evidence of glutamate/monoamine co-release and of mutual exclusivity of serotonin/glutamate and octopamine/glutamate neurons. 

Weaknesses: 

(1) Often, it is mentioned that the expression is higher or lower or regional without quantification or an indication of the number of samples analysed. 

(2) The experiment aimed at tracking sperm in the male reproductive system is difficult to interpret when it is not assessed whether ejaculation has occurred. 

(3) The experiment looking at peristaltic waves in the male organs is missing labeling of the different regions and quantification of the observed waves. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) While the peripheral innervations are very carefully described, it is not clear to which SGNs and OGNs (i.e., cell bodies in the central nervous system) these innervations belong. Are SV, AG, and ED innervated by branches of one neuron or by separate neurons? Multi-color flip-out experiments could provide an answer to this. 

We agree this is important and are planning these experiments for follow-up study.

(2) In contrast, for the analysis of the VT19028 split line (Figure 9), only vnc and cell body images are shown. How do the arborisations of these split combinations look in the periphery? Are the same reproductive organs innervated as shown in Figure 2?

Figure 9S3 was inadvertently omitted from the initial submission.  That figure is now included and shows that the VT019028 split broadly innervates the SV, AG, and ED.

(3) In the discussion, I think it would be helpful to offer some potential explanations for the role of octopaminergic and glutamatergic signaling. If not required for basic fertility, they probably have some other role.

Thank you, we have included speculation in the Discussion section "Potential for adaptation to environment".

(4) Line 543: Figure 8S4 E, (not 8E). 

Correction made.

Reviewer #2 (Recommendations for the authors): 

(1) Line 213-217 

Comment:

The use of "significantly less expression" may be misleading, as no quantification or statistical analysis is provided to support this comparison. 

Suggestion:

Consider using a more neutral term, such as "markedly less" or "noticeably less," unless quantitative data and statistical analysis are included to substantiate the claim.

Good recommendation.This suggestion has been incorporated.

(2) Line 264-267 

Comment:

The observation regarding the distinct morphology of SGNs and OGNs is interesting and could strengthen the argument regarding functional differences. 

Suggestion: 

Consider including a quantification of morphological complexity (e.g., branching) to support the claim. A method such as Sholl analysis (Sholl, 1953), as adapted in Fernández et al., 2008, could be applied. 

This is a good suggestion, and we will consider it as part of a follow-up study.

(3) Line 269-271 

Comment:

The anatomical context of the observation is not explicitly stated. 

Suggestion:

Add "in the ED" for clarity: "With the TRH-GAL4 experiment in the ED, vGlut-40XMYC (Figure 5S1, A and E) and 6XV5-vMAT (Figure 5S1, B and F) were both present with a highly overlapping distribution (Figure 5S1, I)." 

Suggestion has been incorporated.

(4) Line 275-276 

Comment:

The claim about the reduced ability to distinguish SGNs and OGNs in the ED would benefit from quantitative support. 

Suggestion:

Include a morphological comparison or quantification between SGNs and OGNs in the ED and SV to reinforce this point.

Certain information on morphological comparison can be inferred within the images themselves, and we will include quantitation in a follow-up study.

(5) Line 277-279 

Comment:

As with line 269, the anatomical site could be specified more clearly. 

Suggestion: 

Rephrase as: "With the Tdc2-GAL4 experiment in the ED, vGlut-40XMYC (Figure 5S1, M and Q) and 6XV5-vMAT (Figure 5S1, N and R) were both observed in a highly overlapping distribution (Figure 5S1, U)." 

Suggestion has been incorporated.

(6) Line 348-350 

Comment:

The phrase "significantly higher density" implies a statistical comparison that is not shown. 

Suggestion:

If no quantification is provided, replace with a qualitative term such as "visibly higher" or "notably more dense." Alternatively, add a quantitative analysis with statistical testing to justify the use of "significantly." 

Suggestion has been incorporated.

(7) Lines 415-458 (Section comment) 

Comment:

There appears to be differential localization of neurotransmitter receptor expression (glutamate in muscle vs. 5-HT in epithelium or neurons), which could have functional implications. 

Suggestion:

Expand this section to briefly discuss the differential localization patterns of these receptors and potential implications for signal transduction in male reproductive tissues. 

(8) Lines 638-682 (Section comment) 

Comment:

The table summarizing fertility phenotypes would be more informative with additional detail on experimental outcomes. 

Suggestion:

Add a column showing the number of fertile males over the total tested (e.g., "n fertile / n total"). Also, clarify whether the fertility assays are identical to those reported in Figure 10S2, and whether similar analyses were conducted for females. Consider including a figure summarizing fertility results for all genotypes listed in the table, similar to Figure 10S2. 

The fertility tests reported in Table 1 were separate from those reported in Figure 10S2.  For these tests, the results were clear-cut with 100% of males and females reported as infertile exhibiting the infertile phenotype.  For the males and females reported as fertile, it was also clear-cut with nearly 100% showing fertility at a high level.  In subsequent figures we attempted to assess degrees of fertility.

(9) Line 724-727 

Comment:

There seems to be a mistake in the identification of the driver lines used to silence OA neurons. Also, figure references might be incorrect. 

Suggestion:

The OA neuron driver line should be corrected to "Tdc2-GAL4-DBD ∩ AbdB-AD" instead of TRH-GAL4. Additionally, the figure references should be verified; specifically, the letter "B" (in "Figure 10B, D" and "10B, E") appears to be unnecessary or misplaced.

Thanks for catching this, the corrections have been made.

(10) Line 872-877 

Comment:

The discussion on the co-release of fast-acting glutamate and slower aminergic neurotransmitters is interesting and well-articulated. However, it remains somewhat disconnected from the behavioral findings. 

Suggestion:

Consider linking this proposed mechanism to the results observed in the mating duration assays. For instance, the sequential action of neurotransmitters described here could potentially underlie the prolonged mating observed when specific neuromodulators are active, helping to functionally integrate molecular and behavioral data. 

(11) Line 926-928 

Comment:

The interpretation of 5-HT7 receptor expression in the sphincter is compelling, suggesting a role in regulating its function. However, this anatomical observation could be further contextualized with the functional data. 

Suggestion:

It may strengthen the interpretation to explicitly connect this finding with the fertility assays, where SGNs - presumably acting via serotonergic signaling - are shown to be necessary for male fertility. This would support a functional role for 5-HT7 in reproductive success via sphincter regulation.

This has been added. 

(12) Figure 1 

Comment:

The figure legend is generally clear, but could benefit from more consistency and precision in the color-coded labeling. Additionally, the naming of some structures could be more explicit. 

Suggestion: 

Revise the figure and the legend as follows:

Figure 1. The Drosophila male reproductive system. A) Schematic diagram showing paired testes (colour), SVs (green), AGs (purple), Sph (red), ED (gray), and EB (colour). B) Actual male reproductive system. Te - testes, SV - seminal vesicle, AG - accessory gland, Sph - singular sphincter, ED - ejaculatory duct, EB - ejaculatory bulb. Scale bar: 200 µm.

This suggestion has been incorporated.

(13) Figure 3S2 

Comment:

There appears to be a typographical error in the description of the genotypes, which may lead to confusion. 

Suggestion:

Correct the legend to reflect the appropriate genotypes:

Figure 3S2. Expression of vGlut-LexA and Tdc2-GAL4 in the Drosophila male reproductive system. A, D, G, J, M, P) vGlut-LexA, LexAop-6XmCherry; B, E, H, K, N, Q) Tdc2-GAL4, UAS-6XGFP; C, F, I, L, O, R) Overlay. Scale bars: O - 50 µm; R - 10 µm.

The corrections have been made.

(14) Figure 3S3

Comment:

The genotypes for panels D and E appear to be incomplete; the DBD component of the split-GAL4 drivers is missing. 

Suggestion:

Update the figure legend to: 

Figure 3S3. Fruitless and Doublesex expression in the Drosophila male reproductive system. A) fru-GAL4, UAS-6XGFP; B) vGlut-LexA, LexAop-6XmCherry; C) Overlay; D) Tdc2-AD ∩ dsx-GAL4-DBD; E) TRH-AD ∩ dsx-GAL4-DBD. Scale bar: 200 µm.

The corrections have been made.

(15) Figure 4S4 

Comment: 

There is a repeated segment in the figure legend, which makes it unclear and redundant. 

Suggestion:

Edit the legend to remove the duplicated lines: 

Figure 4S4. Expression of vGlut, TβH-GFP, and 5-HT at the junction of the SV and AGs with the ED of the Drosophila male reproductive system. A) vGlut-40XV5; B) TβH-GFP; C) 5-HT; D) vGlut-40XV5, TβH-GFP overlay; E) vGlut-40XV5, 5-HT overlay; F) TβH-GFP, 5-HT overlay. Scale bar: 50 µm.

The correction has been made.

(16) Figure 6S5 

Comment:

Within this figure, the orientation and/or scale of the tissue varies noticeably between individual panels, making it difficult to directly compare the different experimental conditions. 

Suggestion:

For improved clarity and interpretability, consider standardizing the orientation and size of the tissue shown across all panels within the figure. Consistent presentation will facilitate direct comparisons between treatments or genotypes. 

There is often variation in the size of the male reproductive organs. They were all acquired at the same magnification. The only point of this figure is there is no vGAT or vAChT at these NMJs and the result is unambiguously negative. 

(17) Figure 10 

Comment:

Panel A appears redundant, as it shows the same information as the other panels but without indicating statistical significance. 

Suggestion:

Consider removing panel A and keeping only the remaining four graphs, which include relevant statistical comparisons and clearly show significant differences.

We realize there is some redundancy of panel A with the other panels, but we feel there is value in having all the genotypes in a single panel for comparison.

Reviewer #3 (Recommendations for the authors): 

Here are some suggestions to improve the manuscript: 

(1) Prot B GFP experiment: the authors should explain better the time chosen to look at the sperm content of the male reproductive system. At 10 minutes, it is expected that the male has already ejaculated, and therefore, a failure to ejaculate would result in more sperm in the reproductive system, not less. Since we are not certain when the male ejaculates, it would be important to do the analysis at different time points.

In the Prot-GFP experiments, the 10-minute time point was chosen because we nearly always observe sperm in the ejaculatory duct of control males.  In the experimental males, we never observed sperm in the ejaculatory duct at this time point.  Also, no Prot-GFP sperm were observed in the reproductive tract of females mated to experimental males even when mating was allowed to go to completion, while abundant sperm were found in females mated to Prot-GFP controls.  Figure 10S1 has been updated to include Images of these female reproductive systems.  The results showing the absence of Prot-GFP sperm in the female reproductive tract mated to experimental males indicates sperm transfer in these males isn't occurring earlier during the copulation process than in control males and that we didn't miss it by only examining at the ejaculatory duct.

(2) Discuss what may be the role of the octopamine/glutamate neurons and glutamate transmission in serotonin/glutamate neurons in the male reproductive system, given that they are not required for fertility (at least under the context in which it was tested). It is quite a striking result that deserves some attention. 

We agree it is a surprising result and have included speculation on the role of glutamate and octopamine in male reproduction in the Discussion section "Potential for adaptation to environment".

(3) Very important: 

(a) Figure 3 is present in the Word document but not the PDF. 

(b) Figure 9S3 is not present 

(c) In Figure 5 X), the legend does not correspond to the panel.

All of these corrections have been made. 

(4) Other suggestions:

(a) A summary schematic (or several) of the findings would make it an easier read.

(b) Explain why the ejaculatory bulb was left out of the analysis.

(c) Explain in the main text some of the tools, such as, BONT-C and the conditional vGlut mutation.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

In this paper, the authors developed a chemical labeling reagent for P2X7 receptors, called X7-uP. This labeling reagent selectively labels endogenous P2X7 receptors with biotin based on ligand-directed NASA chemistry (Ref. 41). After labeling the endogenous P2X7 receptor with biotin, the receptor can be fluorescently labeled with streptavidin-AlexaFluor647. The authors carefully examined the binding properties and labeling selectivity of X7-uP to P2X7, characterized the labeling site of P2X7 receptors, and demonstrated fluorescence imaging of P2X7 receptors. The data obtained by SDS-PAGE, Western blot, and fluorescence microscopy clearly show that X7-uP labels the P2X7 receptor. Finally, the authors fluorescently labeled the endogenous P2X7 in BV2 cells, which are a murine microglia model, and used dSTORM to reveal a nanoscale P2X7 redistribution mechanism under inflammatory conditions at high resolution. 

Strengths: 

X7-uP selectively labels endogenous P2X7 receptors with biotin. Streptavidin-AlexaFluor647 binds to the biotin labeled to the P2X7 receptor, allowing visualization of endogenous P2X7 receptors. 

We thank the reviewer for their positive comment.

Weaknesses: 

Weaknesses & Comments 

(1) The P2X7 receptor exists in a trimeric form. If it is not a monomer under the conditions of the pull-down assay in Figure 2C, the quantitative values may not be accurate. 

We thank the reviewer for this comment. As shown in Figure 2C, the band observed on the denaturing SDS-PAGE corresponds to the monomeric form of the P2X7 receptor. While we cannot exclude the presence of non-monomeric species under native conditions, no such higher-order forms are visible in the gel. This observation supports the conclusion that the quantitative values presented are based on the monomeric form and are therefore reliable.

(2) In Figure 3, GFP fluorescence was observed in the cell. Are all types of P2X receptors really expressed on the cell surface ? 

We thank the reviewer for this excellent comment, which was also raised by reviewer 2. To address this concern, we performed a commercial cell-surface protein biotinylation assay to assess whether GFP-tagged P2X receptors reach the plasma membrane. As expected, all P2X subtypes except P2X6 were detected at the cell surface in HEK293T cells, thereby validating our confocal fluorescence microscopy assay. These new data are now included in Figure 3 — figure supplement 1.

(3) The reviewer was not convinced of the advantages of the approach taken in this paper, because the endogenous receptor labeling in this study could also be done using conventional antibody-based labeling methods. 

We thank the reviewer for raising this important point and would like to highlight several advantages of our approach compared to conventional antibody-based labeling.

First, commercially available P2X7 antibodies often suffer from poor specificity and are generally not suitable for reliably detecting endogenous P2X7 receptors, as documented in previous studies (e.g., PMID: 16564580 and PMID: 15254086). While recent advances have been made using nanobodies with improved specificity for P2X7 (e.g., PMID: 30074479 and PMID: 38953020), our strategy is distinct and complementary to nanobody-based approaches.

Second, antibodies rely on non-covalent interactions with the receptor, which can result in dissociation over time. In contrast, our X7-uP probe covalently biotinylates lysine residues on the P2X7 receptor through stable amide bond formation. This covalent labeling ensures that the biotin moiety remains permanently attached, an advantage not afforded by reversible binding strategies.

Third, by selectively biotinylating P2X7 receptors, our method provides a versatile platform for the chemical attachment of a wide range of probes or functional moieties. Although we did not demonstrate this application in the current study, we believe this modularity represents an additional advantage of our approach.

We have now revised the discussion to highlight these key advantages, allowing the reader to form their own opinion. We hope this addresses the reviewer’s concerns and clarifies the benefits of our approach.

(4) Although P2X7 was successfully labeled in this paper, it is not new as a chemistry. There is a need for more attractive functional evaluation such as live trafficking analysis of endogenous P2X7. 

We agree with the reviewer that the underlying chemistry is not novel per se. However, to our knowledge, it has not previously been applied to the P2X7 receptor, and thus constitutes a novel application with specific relevance for studying native P2X7 biology.

We also appreciate the reviewer’s suggestion regarding live trafficking analysis of endogenous P2X7. While this is indeed a valuable and interesting direction, we believe it lies beyond the scope of the present study, as it would first require demonstrating that the labeling itself does not affect P2X7 function (see below). This important step would necessitate additional experiments, which we consider more appropriate for a follow-up investigation.

(5) The reviewer has concerns that the use of the large-size streptavidin to label the P2X7 receptor may perturbate the dynamics of the receptor. 

We thank the reviewer for raising this important point. Although we did not directly measure receptor dynamics, it is indeed possible that tetrameric streptavidin (tStrept-A 647) could promote P2X7 clustering by cross-linking nearby receptors due to its tetravalency (see also point 7 raised by the reviewer). To address this concern, we performed additional dSTORM experiments using a monomeric form of streptavidin-Alexa 647 (mSA) (see PMID: 26979420). Owing to its reduced size and lack of tetravalency, mSA has been shown to minimize artificial crosslinking of synaptic receptors (PMID: 26979420). A drawback of using mSA, however, is that the monomeric form carries only two fluorophores (estimated degree of labeling, DOL ≈ 2, PMID: 26979420), whereas the tetrameric form, according to the manufacturer’s certificate of analysis (Invitrogen S21374), has an average DOL of three fluorophores per monomer, resulting in a total of ~12 fluorophores per streptavidin.

We tested three conditions with mSA incubation: (i) control BV2 cells (without X7-uP), (ii) untreated X7-uP-labeled BV2 cells, and (iii) X7-uP-labeled BV2 cells treated with LPS and ATP (using the same concentrations and incubation times described in the manuscript). As shown in Author response image 1, only LPS+ATP treatment induced a clear increase in the mean cluster density compared to quiescent (untreated) BV2 cells. This effect closely matches the results obtained with tStrept-A 647, supporting the conclusion the tetrameric streptavidin does not artificially promote P2X7 clustering. It is also possible that the cellular environment of BV2 microglia differs from the confined architecture of synapses, which may further explain why cross-linking effects are less pronounced in our system.

As expected, the overall fluorescence signal with mSA was about tenfold lower than with tStrept-A 647, consistent with the expected fluorophore stoichiometry. This lower signal may explain why the values for the untreated condition appeared slightly higher than for the control, although the difference was not statistically significant (P = 0.1455).

We hope these additional experiments adequately address the reviewer’s concerns.

Author response image 1.

BV2 labeling with monomeric streptavidin–Alexa 647 (mSA).(A) Bright-field and dSTORM images of BV2 cells labeled with mSA in the presence (untreated and LPS+ATP) or absence (control) of 1 µM X7-uP. Treatment: LPS (1 µg/mL for 24 hours) and ATP (1 mM for 30 minutes). Scale bars, 10 µm. Insets: Magnified dSTORM images. Scale bars, 1 µm.(B) Quantification of the number of localizations (n = 2 independent experiments). Bars represent mean ± s.e.m. One-way ANOVA with Tukey’s multiple comparisons (P values are indicated above the graph).

(6) It is better to directly label Alexa647 to the P2X7 receptor to avoid functional perturbation of P2X7. 

Directly labeling of Alexa647 to the P2X7 receptor would require the design and synthesis of a novel probe, which is currently not available. Implementing such a strategy would involve substantial new experimental work that lies beyond the scope of the present study.

(7) In all imaging experiments, the addition of streptavidin, which acts as a cross-linking agent, may induce P2X7 receptor clustering. This concern would be dispelled if the receptors were labeled with a fluorescent dye instead of biotin and observed. 

We refer the reviewer to our response in point 5, where we addressed this concern by comparing tetrameric and monomeric streptavidin conjugates. As noted above (see also point 6), directly labeling the receptor with a fluorescent dye would require the development of a new probe, which is outside the scope of the present study.

(8) There are several mentions of microglia in this paper, even though they are not used. This can lead to misunderstanding for the reader. The author conducted functional analysis of the P2X7 receptor in BV-2 cells, which are a model cell line but not microglia themselves. The text should be reviewed again and corrected to remove the misleading parts that could lead to misunderstanding. e.g. P8. lines 361-364

First, it combines N-cyanomethyl NASA chemistry with the high-affinity AZ10606120 ligand, enabling rapid labeling in microglia (within 10 min)

P8. lines 372-373 

Our results not only confirm P2X7 expression in microglia, as previously reported (6, 26-33), but also reveal its nanoscale localization at the cell surface using dSTORM. 

We agree with the reviewer’s comment. We have now modified the text, including the title.

Reviewer #2 (Public review): 

Summary: 

In this manuscript, Arnould et. al. develop an unbiased, affinity-guided reagent to label P2X7 receptor and use super-resolution imaging to monitor P2X7 redistribution in response to inflammatory signaling. 

Strengths: 

I think the X7-uP probe that they developed is very useful for visualizing localization of P2X7 receptor. They convincingly show that under inflammatory conditions, there is a reorganization of P2X7 localization into receptor clusters. Moreover, I think they have shown a very clever way to specifically label any receptor of interest. This has broad appeal 

We thank the reviewer for their positive comment.

Weaknesses: 

Overall, the manuscript is novel and interesting. However, I do have some suggestions for improvement. 

(1) While the authors state that chemical modification of AZ10606120 to produce the X7-UP reagent has "minimal impact" on the inhibition of P2X7, we can see from Figure 2A and 2B that it does not antagonize P2X7 as effectively as the original antagonist. For the sake of completeness and quantitation, I think it would be great if the authors could determine the IC50 for X7-uP and compare it to the IC50 of AZ10606120. 

We thank the reviewer for this insightful comment. Unfortunately, due to the limited availability of X7-uP, we were not able to establish a complete concentration–response curve to determine its IC₅₀, which would require testing at concentrations >1 µM. Nevertheless, to estimate the effect of the modification, we assessed current inhibition at 300 µM X7-uP and compared it with the reported IC₅₀ of AZ10606120 (10 nM). Under these conditions, both compounds produced a similar level of inhibition, indicating that while the chemical modification reduces potency relative to AZ10606120, X7-uP still functions as an effective probe for P2X7. We have now included these data in Figure 2 and revised the text accordingly.

(2) Do the authors know whether modification of the lysines with biotin affects the receptor's affinity for ATP (or ability to be activated by ATP)? What about P2X7 that has been modified with biotin and then labeled with Alexa 647? For the sake of completeness and quantitation, I think it would be great if the authors could determine the EC50 of biotinylated P2X7 for ATP as well as biotinylated and then Alexa 647 labeled P2X7 for ATP and compare these values to the affinity of unmodified WT P2X7 for ATP.

We thank the reviewer for raising this important point. At present, we have not determined whether modification of lysine residues with biotin, or subsequent labeling with Alexa647, affects the ATP sensitivity or functional properties of P2X7. However, we believe this does not impact the conclusions of the current study, as all functional assays were conducted prior to X7-uP labeling. The labeling is used here as a terminal "snapshot" to visualize the endogenous receptor without interfering with the functional characterization.

We fully agree that assessing the functional integrity of P2X7 following biotinylation and fluorophore labeling—such as by determining the EC₅₀ for ATP—would be essential for studies involving dynamic or post-labeling functional analyses, such as live trafficking. However, as noted earlier in our response to Reviewer 1 (point 4), these experiments lie beyond the scope of the current study.

(3) It is a little misleading to color the fluorescence signal from mScarlet green (for example, in Figure 3 and Figure 4). The fluorescence is not at the same wavelength as GFP. In fact, the wavelength (570 nm - 610 nm) for emission is closer to orange/red than to green. I think this color should be changed to differentiate the signal of mScarlet from the GFP signal used for each of the other P2X receptor subtypes. 

As suggested, we changed the mScarlet color to orange for all relevant figures.

(4) It is my understanding that P2X6 does not form homotrimers. Thus, I was a little surprised to see that the density and distribution of P2X6-GFP in Figure 3 looks very similar to the density and distribution of the other P2X subtypes. Do the authors have an explanation for this? Are they looking at P2X6 protomers inserted into the plasma membrane? Does the cell line have endogenous P2X receptor subtypes? Is Figure 3 showing heterotrimers with P2X6 receptor? A little explanation might be helpful.

We thank the reviewer for raising this important point. Indeed, it is well established that P2X6 does not form functional channels, which supports the conclusion that it does not form homotrimeric complexes. Although previous studies have shown that P2X6–GFP expression is generally lower, more diffuse, and not efficiently targeted to the cell surface compared with other P2X subtypes (see PMID: 12077178), the similar fluorescence distribution and density observed in our Figure 3 do not imply that P2X6 forms homotrimers.

We did not directly assess the presence of endogenous P2X6 in our HEK293T cells; however, according to the Human Protein Atlas, there is no detectable P2X6 RNA expression in HEK293 cells (nTPM = 0), indicating that endogenous P2X6 is not expressed in this cell line. To further investigate surface expression (see also point 2 of reviewer 1), we performed a commercial cell-surface protein biotinylation assay to assess whether GFP-tagged P2X6 reaches the plasma membrane. As expected, P2X6 was not detected at the cell surface in HEK293T cells, whereas GFP-tagged P2X1 to P2X5 were readily detected. These results further support the conclusion that P2X6 does not insert into the plasma membrane as a homotrimer, thereby validating our confocal fluorescence microscopy assay. These new data are now included in Figure 3 — figure supplement 1.

(5) It is easy to overlook the fact that the antagonist leaves the binding pocket once the biotin has been attached to the lysines. It might be helpful if the authors made this a little more apparent in Figure 1 or in the text describing the NASA chemistry reaction.

We thank the reviewer for this insightful suggestion. To address this, we have modified Figure 1A and updated the legend.

Reviewer #3 (Public review): 

Summary: 

This manuscript describes the development of a covalent labeling probe (X7-uP) that selectively targets and tags native P2X7 receptors at the plasma membrane of BV2 microglial cells. Using super-resolution imaging (dSTORM), the authors demonstrate that P2X7 receptors form nanoscale clusters upon microglial activation by lipopolysaccharide (LPS) and ATP, correlating with synergistic IL-1β release. These findings advance understanding of P2X7 reorganization during inflammation and provide a generalizable labeling strategy for monitoring endogenous P2X7 in immune cells. 

Strengths: 

(1) The authors designed X7-uP by coupling a high-affinity, P2X7-specific antagonist (AZ10606120) with N-cyanomethyl NASA chemistry to achieve site-directed biotinylation. This approach offers high specificity, minimal off-target reactivity, and a straightforward pull-down/imaging readout. 

(2) The results connect P2X7's nanoscale clustering directly with IL-1β secretion in microglia, reinforcing the role of P2X7 in inflammation. By localizing endogenous P2X7 at single-molecule resolution, the authors reveal how LPS priming and ATP stimulation synergistically reorganize the receptor. 

(3) The authors systematically validate their method in recombinant systems (HEK293 cells) and in BV2 cells, showing selective inhibition, mutational confirmation of the binding site, and Western blot pulldown experiments.

We thank the reviewer for their positive comment.

Weaknesses: 

(1) While the data strongly indicate that P2X7 clustering contributes to IL-1β release, the manuscript would benefit from additional experiments (if feasible) or discussion on how receptor clustering interfaces with downstream inflammasome assembly. Clarification of whether the P2X7 clusters physically colocalize with known inflammasome proteins would solidify the mechanism. 

We thank the reviewer for this valuable suggestion. Determining the physical colocalization of P2X7 clusters with known inflammasome components would provide important insight into the molecular partners involved in inflammasome activation. However, we believe that such an investigation would constitute a substantial study on its own and therefore lies beyond the scope of the present work.

Nevertheless, in response to the reviewer’s suggestion, we have added a short paragraph at the end of the Discussion section addressing potential mechanisms by which P2X7 clustering may contribute to downstream inflammasome activation. We also revised the text to tone down the hypothesis of physical colocalization.

(2) The authors might expand on the scope of X7-uP in other native cells that endogenously express P2X7 (e.g., macrophages, dendritic cells). Although they mention the possibility, demonstrating the probe's applicability in at least one other primary immune cell type would strengthen its general utility. 

We thank the reviewer for this valuable suggestion. Again, we believe that such an investigation would constitute a substantial study on its own and therefore lies beyond the scope of the present work.

(3) The authors do include appropriate negative controls, yet providing additional details (e.g., average single-molecule on-time or blinking characteristics) in supplementary materials could help readers assess cluster calculations. 

As suggested, we have included additional data showing single-molecule blinking events in untreated and LPS+ATP-treated BV2 cells, along with the corresponding movies. The data are now presented in Figure 5—supplement figure 3A and B and Figure 5—Videos 1 and 2.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors): 

(1) On line 96, the authors refer to the "ballast" domain of P2X7 receptor but do not cite the original article from which this nomenclature originated (McCarthy et al., 2019, Cell). This article should be cited to give appropriate credit. 

Done.

(2) On line 602, the authors state that they use models from PDB 1MK5 and 6U9W to generate the cartoons in Figure 6. The manuscripts from which these PDB files were generated need to be appropriately cited. 

Done.

(3) On line 319, the authors say "300 mM BzATP" but I think they mean 300 uM.

Done. Thank you for catching the typo.

Reviewer #3 (Recommendations for the authors): 

Overall, excellent data quality. The paper would benefit from a discussion of the physiological implications of clustering. It would also be helpful to elaborate about the potential mechanisms for clustering: diffusion and/or insertion. Finally, the authors should comment on work by Mackinnon's (PMID: 39739811) and Santana lab (PMID: 31371391) on two distinct models for clustering of proteins. 

As suggested by the reviewer, we have revised the discussion to incorporate their comments. First, we have added the following text:

“Upon BV2 activation, we observed significant nanoscale reorganization of P2X7. Both LPS and ATP (or BzATP) trigger P2X7 upregulation and clustering, increasing the overall number of surface receptors and the number of receptors per cluster, from one to three (Figure 6). By labeling BV2 cells with X7-uP shortly after IL-1b release, we were able to correlate the nanoscale distribution of P2X7 with the functional state of BV2 cells, consistent with the two-signal, synergistic model for IL-1b secretion observed in microglia and other cell types (Ferrari et al, 1996; Perregaux et al, 2000; Ferrari et al, 2006; Di Virgilio et al, 2017; He et al, 2017; Swanson et al, 2019). In this model, LPS priming leads to intracellular accumulation of pro-IL-1b, while ATP stimulation activates P2X7, triggering NLRP3 inflammasome activation and the subsequent release of mature IL-1b.

What is the mechanism underlying P2X7 upregulation that leads to an overall increase in surface receptors—does it result from the lateral diffusion of previously masked receptors already present at the plasma membrane, or from the insertion of newly synthesized receptors from intracellular pools in response to LPS and ATP? Although our current data do not distinguish between these possibilities, a recent study suggests that the a1 subunit of the Na⁺/K</sup>+</sup>-ATPase (NKAa1) forms a complex with P2X7 in microglia, including BV2 cells, and that LPS+ATP induces NKAa1 internalization (Huang et al, 2024). This internalization appears to release P2X7 from NKAa1, allowing P2X7 to exist in its free form. We speculate that the internalization of NKAa1 induced by both LPS and ATP exposes previously masked P2X7 sites, including the allosteric AZ10606120 sites, thus making them accessible for X7-uP labeling.”

Second, we have added a short paragraph at the end of the Discussion section addressing potential mechanisms by which P2X7 clustering may contribute to downstream inflammasome activation:

“What mechanisms underlie P2X7 clustering in response to inflammatory signals? Several models have been proposed to explain membrane protein clustering, including recruitment to structural scaffolds (Feng & Zhang, 2009), partitioning into membrane domains enriched in specific chemical components such as lipid rafts (Simons & Ikonen, 1997), and self-assembly mechanisms (Sieber et al, 2007). These self-assembly mechanisms include an irreversible stochastic model (Sato et al, 2019) and a more recent reversible self-oligomerization model which gives rise to higher-order transient structures (HOTS) (Zhang et al, 2025). Supported by cryogenic optical localization microscopy with very high resolution (~5 nm), the HOTS model has been observed in various membrane proteins, including ion channels and receptors (Zhang et al, 2025). Furthermore, HOTS are suggested to be dynamically modulated and to play a functional role in cell signaling, potentially influencing both physiological and pathological processes (Zhang & MacKinnon, 2025). While this hypothesis is compelling, our current dSTORM data lack sufficient spatial resolution to confirm whether P2X7 trimers form HOTS via self-oligomerization. Further biophysical and ultra-high-resolution imaging studies are required to test this model in the context of P2X7 clustering.”

Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public review):

Summary:

This manuscript by Pournejati et al investigates how BK (big potassium) channels and CaV1.3 (a subtype of voltage-gated calcium channels) become functionally coupled by exploring whether their ensembles form early-during synthesis and intracellular trafficking-rather than only after insertion into the plasma membrane. To this end, the authors use the PLA technique to assess the formation of ion channel associations in the different compartments (ER, Golgi or PM), single-molecule RNA in situ hybridization (RNAscope), and super-resolution microscopy.

Strengths:

The manuscript is well written and addresses an interesting question, combining a range of imaging techniques. The findings are generally well-presented and offer important insights into the spatial organization of ion channel complexes, both in heterologous and endogenous systems.

Weaknesses:

The authors have improved their manuscript after revisions, and some previous concerns have been addressed.

Still, the main concern about this work is that the current experiments do not quantitatively or mechanistically link the ensembles observed intracellularly (in the endoplasmic reticulum (ER) or Golgi) to those found at the plasma membrane (PM). As a result, it is difficult to fully integrate the findings into a coherent model of trafficking. Specifically, the manuscript does not address what proportion of ensembles detected at the PM originated in the ER. Without data on the turnover or halflife of these ensembles at the PM, it remains unclear how many persist through trafficking versus forming de novo at the membrane. The authors report the percentage of PLApositive ensembles localized to various compartments, but this only reflects the distribution of pre-formed ensembles. What remains unknown is the proportion of total BK and Ca_V1.3 channels (not just those in ensembles) that are engaged in these complexes within each compartment. Without this, it is difficult to determine whether ensembles form in the ER and are then trafficked to the PM, or if independent ensemble formation also occurs at the membrane. To support the model of intracellular assembly followed by coordinated trafficking, it would be important to quantify the fraction of the total channel population that exists as ensembles in each compartment. A comparable ensemble-to-total ratio across ER and PM would strengthen the argument for directed trafficking of pre-assembled channel complexes.

We appreciate the reviewer’s thoughtful comment and agree that quantitatively linking intracellular hetero-clusters to those at the plasma membrane is an important and unresolved question. Our current study does not determine what proportion of ensembles at the plasma membrane originated during trafficking. It also does not quantify the fraction of total BK and Ca_V1.3 channels engaged in these complexes within each compartment. Addressing this requires simultaneous measurement of multiple parameters—total BK channels, total Ca_V1.3 channels, hetero-cluster formation (via PLA), and compartment identity—in the same cell. This is technically challenging. The antibodies used for channel detection are also required for the proximity ligation assay, which makes these measurements incompatible within a single experiment.

To overcome these limitations, we are developing new genetically encoded tools to enable real-time tracking of BK and Ca_V1.3 dynamics in live cells. These approaches will enable us to monitor channel trafficking and the formation of hetero-clusters, as detected by colocalization. This kind of experiments will provide insight into their origin and turnover. While these experiments are beyond the scope of the current study, the findings in our current manuscript provide the first direct evidence that BK and CaV channels can form hetero-clusters intracellularly prior to reaching the plasma membrane. This mechanistic insight reveals a previously unrecognized step in channel organization and lays the foundation for future work aimed at quantifying ensemble-to-total ratios and determining whether coordinated trafficking of pre-assembled complexes occurs.

This limitation is acknowledged in the discussion section, page 23. It reads: “Our findings highlight the intracellular assembly of BK-Ca_V1.3 hetero-clusters, though limitations in resolution and organelle-specific analysis prevent precise quantification of the proportion of intracellular complexes that ultimately persist on the cell surface.”

Reviewer #2 (Public review):

Summary:

The co-localization of large conductance calcium- and voltage activated potassium (BK) channels with voltage-gated calcium channels (CaV) at the plasma membrane is important for the functional role of these channels in controlling cell excitability and physiology in a variety of systems.

An important question in the field is where and how do BK and CaV channels assemble as 'ensembles' to allow this coordinated regulation - is this through preassembly early in the biosynthetic pathway, during trafficking to the cell surface or once channels are integrated into the plasma membrane. These questions also have broader implications for assembly of other ion channel complexes

Using an imaging based approach, this paper addresses the spatial distribution of BKCaV ensembles using both overexpression strategies in tsa201 and INS-1 cells and analysis of endogenous channels in INS-1 cells using proximity ligation and superesolution approaches. In addition, the authors analyse the spatial distribution of mRNAs encoding BK and Cav1.3.

The key conclusion of the paper that BK and Ca_V1.3 are co-localised as ensembles intracellularly in the ER and Golgi is well supported by the evidence.However, whether they are preferentially co-translated at the ER, requires further work. Moreover, whether intracellular pre-assembly of BK-Ca_V1.3 complexes is the major mechanism for functional complexes at the plasma membrane in these models requires more definitive evidence including both refinement of analysis of current data as well as potentially additional experiments.

The reviewer raises the question of whether BK and Ca_V1.3 channels are preferentially co-translated. In fact, I would like to propose that co-translation has not yet been clearly defined for this type of interaction between ion channels. In our current work, we 1) observed the colocalization between BK and Ca_V1.3 mRNAs and 2) determined that 70% of BK mRNA in active translation also colocalizes with Ca_V1.3 mRNA. We think these results favor the idea of translational complexes that can underlie the process of co-translation. However, and in total agreement with the Reviewer, the conclusion that the mRNA for the two ion channels is cotranslated would require further experimentation. For instance, mRNA coregulation is one aspect that could help to define co-translation. 

To avoid overinterpretation, we have revised the manuscript to remove references to “co-translation” in the Results section and included the word “potential” when referring to co-translation in the Discussion section. We also clarified the limitations of our evidence in the Discussion that can be found on page 25: “It is important to note that while our data suggest mRNA coordination, additional experiments are required to directly assess co-translation.”

Strengths & Weaknesses

(1) Using proximity ligation assays of overexpressed BK and CaV1.3 in tsa201 and INS1 cells the authors provide strong evidence that BK and CaV can exist as ensembles (ie channels within 40 nm) at both the plasma membrane and intracellular membranes, including ER and Golgi. They also provide evidence for endogenous ensemble assembly at the Golgi in INS-1 cells and it would have been useful to determine if endogenous complexes are also observe in the ER of INS-1 cells. There are some useful controls but the specificity of ensemble formation would be better determined using other transmembrane proteins rather than peripheral proteins (eg Golgi 58K).

We thank the reviewer for their thoughtful feedback and for recognizing the strength of our proximity ligation assay data supporting BK–Ca_V1.3 hetero-clusters formation at both the plasma membrane and intracellular compartments. As for specificity controls, we appreciate the suggestion to use transmembrane markers. To strengthen our conclusion, we have performed an additional experiment comparing the number of PLA puncta formed by the interaction of Ca_V1.3 and BK channels with the number of PLA puncta formed by the interaction of Ca_V1.3 channels and ryanodine receptors in INS-1 cells. As shown in the figure below, the number of interactions between Ca_V1.3 and BK channels is significantly higher than that between Ca_V1.3 and RyR₂. Of note, RyR₂ is a protein resident of the ER. These results provide additional evidence of the existence of endogenous complex formation in INS-1 cells. We have added this figure as a supplement.

(2) Ensemble assembly was also analysed using super-resolution (dSTORM) imaging in INS-1 cells. In these cells only 7.5% of BK and CaV particles (endogenous?) co-localise that was only marginally above chance based on scrambled images. More detailed quantification and validation of potential 'ensembles' needs to be made for example by exploring nearest neighbour characteristics (but see point 4 below) to define proportion of ensembles versus clusters of BK or Cav1.3 channels alone etc. For example, it is mentioned that a distribution of distances between BK and Cav is seen but data are not shown.

We thank the reviewer for this comment. To address the request for more detailed quantification and validation of ensembles, we performed additional analyses:

Proportion of ensembles vs isolated clusters: We quantified clusters within 200 nm and found that 37 ± 3% of BK clusters are near one or more CaV1.3 clusters, whereas 15 ± 2% of CaV1.3 clusters are near BK clusters. Figure 8– Supplementary 1A

Distance distribution: As shown in Figure 8–Supplementary 1B, the nearestneighbor distance distribution for BK-to-CaV1.3 in INS-1 cells (magenta) is shifted toward shorter distances compared to randomized controls (gray), supporting preferential localization of BK–CaV1.3 hetero-clusters.

Together, these analyses confirm that BK–CaV1.3 ensembles occur more frequently than expected by chance and exhibit an asymmetric organization favoring BK proximity to CaV1.3 in INS-1 cells. We have included these data and figures in the revised manuscript, as well as description in the Results section. 

(3) The evidence that the intracellular ensemble formation is in large part driven by cotranslation, based on co-localisation of mRNAs using RNAscope, requires additional critical controls and analysis. The authors now include data of co-localised BK protein that is suggestive but does not show co-translation. Secondly, while they have improved the description of some controls mRNA co-localisation needs to be measured in both directions (eg BK - SCN9A as well as SCN9A to BK) especially if the mRNAs are expressed at very different levels. The relative expression levels need to be clearly defined in the paper. Authors also use a randomized image of BK mRNA to show specificity of co-localisation with Cav1.3 mRNA, however the mRNA distribution would not be expected to be random across the cell but constrained by ER morphology if cotranslated so using ER labelling as a mask would be useful?

We thank the reviewer for these constructive suggestions. We measured mRNA colocalization in both directions as recommended. As shown in the figure below, colocalization between KCNMA1 and SCN9A transcripts was comparable in both directions, with no statistically significant difference, supporting the specificity of the observed associations. We decided not to add this to the original figure to keep the figure simple. 

We agree that co-localization of BK protein with BK mRNA is not conclusive evidence of co-translation, and we do not intend to mislead readers in our conclusion. Consequently, we were careful in avoiding the use of co-translation in the result section and added the word “potential” when referring to co-translation in the Discussion section. We added a sentence in the discussion to caution our interpretation: “It is important to note that while our data suggest mRNA coordination, additional experiments are required to directly assess cotranslation.”

Author response image 1.

(4) The authors attempt to define if plasma membrane assemblies of BK and CaV occur soon after synthesis. However, because the expression of BK and CaV occur at different times after transient transfection of plasmids more definitive experiments are required. For example, using inducible constructs to allow precise and synchronised timing of transcription. This would also provide critical evidence that co-assembly occurs very early in synthesis pathways - ie detecting complexes at ER before any complexes 

We appreciate the reviewer’s insightful suggestion regarding the use of inducible constructs to synchronize transcription timing. This is an excellent approach and would allow direct testing of whether co-assembly occurs early in the synthesis pathway, including detection of complexes at the ER prior to plasma membrane localization. These experiments are beyond the scope of the present work but represent an important direction for future studies.

We have added the following sentence to the Discussion section (page 24) to highlight this idea. “Future experiments using inducible constructs to precisely control transcription timing will enable more precise quantification of heterocluster formation in the ER compartment prior to plasma membrane insertion and reduce the variability introduced by differences in expression timing after plasmid transfection.” 

(5) While the authors have improved the definition of hetero-clusters etc it is still not clear in superesolution analysis, how they separate a BK tetramer from a cluster of BK tetramers with the monoclonal antibody employed ie each BK channel will have 4 binding sites (4 subunits in tetramer) whereas Cav1.3 has one binding site per channel. Thus, how do authors discriminate between a single BK tetramer (molecular cluster) with potential 4 antibodies bound compared to a cluster of 4 independent BK channels.

We appreciate the reviewer’s thoughtful comment regarding the interpretation of super-resolution data. We agree that distinguishing a single BK tetramer from a cluster of multiple BK channels is challenging when using an antibody that can bind up to four sites per channel. To clarify, our analysis does not attempt to resolve individual subunits within a tetramer; rather, it focuses on the nanoscale spatial proximity of BK and Ca_V1.3 signals.

We want to note that this limitation applies only to the super-resolution maps in Figures 8C and 9D and does not affect Airyscan-based analyses or measurements of BK–Ca_V1.3 proximity.

To address how we might distinguish between a single BK tetramer and a cluster of multiple BK channels, we considered two contrasting scenarios. In the first case, we assume that all four α-subunits within a tetramer are labeled. Based on cryoEM structures, a BK tetramer measures approximately 13 nm × 13 nm (≈169 nm²). Adding two antibody layers (primary and secondary) would increase the footprint by ~14 nm in each direction, resulting in an estimated area of ~41 nm × 41 nm (≈1681 nm²). Under this assumption, particles smaller than ~1681 nm² would likely represent individual tetramers, whereas larger particles would correspond to clusters of multiple tetramers. 

In the second scenario, we propose that steric constraints at the S9–S10 segment, where the antibody binds, limit labeling to a single antibody per tetramer. If true, the localization precision would approximate 14 nm × 14 nm—the combined size of the antibody complex and the channel—close to the resolution limit of the microscope. To test this, we performed a control experiment using two antibodies targeting the BK C-terminal domain, raised in different species and labeled with distinct fluorophores. Super-resolution imaging revealed that only ~12% of particles were colocalized, suggesting that most channels bind a single antibody.

If multiple antibodies could bind each tetramer, we would expect much greater colocalization.

Although these data are not included in the manuscript, we have added the following clarification to the Results section (page 19): “It is important to note that this technique does not allow us to distinguish between labeling of four BK αsubunits within a tetramer and labeling of multiple BK channel clusters. Hence, particles smaller than ~1680 nm² may represent either a single tetramer or a cluster. This limitation applies to Figures 8C and 9D and does not affect measurements of BK–Ca_V1.3 proximity.”

Author response image 2.

(6) The post-hoc tests used for one way ANOVA and ANOVA statistics need to be defined throughout

We thank the reviewer for highlighting the need for clarity regarding our statistical analyses. We have now specified the post-hoc tests used for all one-way ANOVA and ANOVA comparisons throughout the manuscript, and updated figure legends.

Reviewer #3 (Public review):

Summary:

The authors present a clearly written and beautifully presented piece of work demonstrating clear evidence to support the idea that BK channels and Cav1.3 channels can co-assemble prior to their assertion in the plasma membrane.

Strengths:

The experimental records shown back up their hypotheses and the authors are to be congratulated for the large number of control experiments shown in the ms.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have sufficiently addressed the specific points previously raised and the manuscript has improved clarity in those aspects. My main concern, which still remains, is stated in the public review.

Reviewer #3 (Recommendations for the authors):

I am content that the authors have attempted to fully address my previous criticisms.

I have only three suggestions

(1) I think the word Homo-clusters at the bottom right of Figure 1 is erroneously included.

We thank the reviewer for bringing this to our attention. The figure has been corrected accordingly.

(2) The authors should, for completeness, to refer to the beta, gamma and LINGO subunit families in the Introduction and include appropriate references:

Knaus, H. G., Folander, K., Garcia-Calvo, M., Garcia, M. L., Kaczorowski, G. J., Smith, M., & Swanson, R. (1994). Primary sequence and immunological characterization of betasubunit of high conductance Ca2+-activated K+ channel from smooth muscle. The Journal of Biological Chemistry, 269(25), 17274-17278.

Brenner, R., Jegla, T. J., Wickenden, A., Liu, Y., & Aldrich, R. W. (2000a). Cloning and functional characterization of novel large conductance calcium-activated potassium channel beta subunits, hKCNMB3 and hKCNMB4. The Journal of Biological Chemistry, 275(9), 6453-6461.

Yan, J & R.W. Aldrich. (2010) LRRC26 auxiliary protein allows BK channel activation at resting voltage without calcium. Nature. 466(7305):513-516

Yan, J & R.W. Aldrich. (2012) BK potassium channel modulation by leucine-rich repeatcontaining proteins. Proceedings of the National Academy of Sciences 109(20):7917-22

Dudem, S, Large RJ, Kulkarni S, McClafferty H, Tikhonova IG, Sergeant, GP, Thornbury, KD, Shipston, MJ, Perrino BA & Hollywood MA (2020). LINGO1 is a novel regulatory subunit of large conductance, Ca2+-activated potassium channels. Proceedings of the National Academy of Sciences 117 (4) 2194-2200

Dudem, S., Boon, P. X., Mullins, N., McClafferty, H., Shipston, M. J., Wilkinson, R. D. A., Lobb, I., Sergeant, G. P., Thornbury, K. D., Tikhonova, I. G., & Hollywood, M. A. (2023). Oxidation modulates LINGO2-induced inactivation of large conductance, Ca2+-activated potassium channels. The Journal of Biological Chemistry, 299 (3) 102975.

We agree with the reviewer’s suggestion and have revised the Introduction to include references to the beta, gamma, and LINGO subunit families. Appropriate citations have been added to ensure completeness and contextual relevance.

Additionally, BK channels are modulated by auxiliary subunits, which fine-tune BK channel gating properties to adapt to different physiological conditions. The β, γ, and LINGO1 subunits each contribute distinct structural and regulatory features: β-subunits modulate Ca²⁺ sensitivity and can induce inactivation; γ-subunits shift voltage-dependent activation to more negative potentials; and LINGO1 reduces surface expression and promotes rapid inactivation (18-24). These interactions ensure precise control over channel activity, allowing BK channels to integrate voltage and calcium signals dynamically in various cell types.

(3) I think it may be more appropriate to include the sentence "The probes against the mRNAs of interest and tested in this work were designed by Advanced Cell Diagnostics." (P16, right hand column, L12-14) in the appropriate section of the Methods, rather than in Results.

We thank the reviewer for this helpful suggestion. In response, we have relocated the sentence to the appropriate section of the Methods, where it now appears with relevant context.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

Summary:

The manuscript titled "Unravelling the Progression of the Zebrafish Primary Body Axis with Reconstructed Spatiotemporal Transcriptomics" presents a comprehensive analysis of the development of the primary body axis in zebrafish by integrating bulk RNA-seq, 3D images, and Stereo-Seq. The authors first clearly demonstrate the application of Palette for integrating RNA-seq and Stereo-Seq using published spatial transcriptomics data of Drosophila embryos. Subsequently, they produced serial bulk RNA-seq data for certain developmental stages of Danio rerio embryos and utilized published Stereo-Seq data. Through robust validation, the authors observe the molecular network involved in AP axis formation. While the authors show that integrating bulk RNA-seq data with Stereo-Seq improves spatial resolution, additional proof is required to demonstrate the extent of this improvement.

Response: We thank the reviewer for the positive feedback on our Palette pipeline, zSTEP construction and analysis of primary body axis development. We appreciate the constructive suggestions provided, which we can implement to improve our manuscript. As pointed out by the reviewer, some analysis procedures were not described in sufficient detail. To address this, we have added more explanatory texts and additional schematic diagrams to make the methods clearer and more understandable. We also thank the reviewer for the meticulous reading and for reminding us to include parameters, references and essential texts, which significantly improve the manuscript quality and make the manuscript more rigorous. Furthermore, as suggested by the reviewer, the extent of the improvement on the spatial resolution was not clearly demonstrated in the manuscript. Therefore, we have provided an additional figure to show the original expression on the stacked Stereo-seq slices and 3D live image compared to the expression from zSTEP, and the results indicate that zSTEP provides better, more continuous expression patterns. We still have two remaining tasks that are expected to be completed within the next month. We hope our responses have address the concerns raised by the reviewer, and we are pleased to provide any additional proof as needed.

Major Comments:

1. Lines 66-68: Discuss the limitations of existing tools and explicitly state the advantages of using Palette.

Response: We thank the reviewer for the valuable suggestion. We have added the following new texts after line 68 to emphasize the features and advantages of Palette.

"Newly developed tools are committed to integrating bulk and/or scRNA-seq data with ST data to enhance spatial resolution, focusing on expression at the spot level. However, gene expression patterns are closely correlated to the biological functions and are more critical for understanding biological processes. Therefore, a tool focusing on inferring spatial gene expression patterns would be desirable."

1. Body Pattern Genes Analysis: For both Drosophila and Danio rerio, it would be valuable to examine body pattern genes in Stereo-Seq and apply Palette to determine if the resolution of the segments improves or merges. The resolution of the A-P axis is convincing, but further evidence for other segments would be beneficial.

Response: We thank the reviewer for the suggestions. For the Drosophila data, we only used two adjacent slices for Palette performance assessment, and thus were only able to evaluate the expression patterns within the slice.

For the zebrafish data, although we have construct zSTEP as a 3D transcriptomic atlas, we have to admit that the left-right (LR) and dorsal-ventral (DV) patterning is not satisfactory enough. Here we show a section from the dorsal part of 16 hpf zSTEP that displays a relatively well-defined left-right pattern (Fig. 2). Along the left-right axis, the notochord cells are centrally located, flanked by somite cells on either side, with the outermost cells being pronephros.

One reason for the limited LR and DV patterning is that the original annotation of the ST data does not clearly distinguish all the cell types. Another reason is likely due to the disordered cell positions when stacking ST slices. Thus, our zSTEP is most suitable for investigating the AP patterns, while the performances on LR and DV patterns may not achieve the same level of accuracy.

See response letter for the figure.

1. Figure 2d: Include the A-P line for which the intensity profile was plotted in the main figure, rather than just in the supplementary material. Additionally, consider simplifying the plot by not combining three lines into one, as it complicates the interpretation of observations.

Response: We thank the reviewer for the helpful suggestions. We have updated Figure 2d and Figure S1b by adding a A-P line on each subfigure (Fig. 3). Additionally, as the reviewer suggested, we have separated the intensity plots so that each subfigure now includes a dedicated intensity plot along A-P axis.

See response letter for the figure.

1. Drosophila Data Analysis: While the alignment and validation of Danio rerio sections are clearly explained, the analysis and validation of Drosophila data are insufficiently detailed. Provide a more thorough explanation of how the intensity profiles between BDGP in situ data and Stereo-Seq data are adjusted.

Response: We thank the reviewer for raising this issue. To make the analysis procedure clearer, we have updated Figure 2a (Fig. 4) and added explanatory texts in the figure legends to describe the processing procedure for the Drosophila ST data.

See response letter for the figure.

Additionally, the following sentences have been added into the Methods section to describe the generation of the intensity profiles.

"The intensity plot profiles along AP axis were generated through the following steps: The expression pattern plot images or in situ hybridization images were imported into ImageJ and converted to grayscale. The colour was then inverted, and a line of a certain width (here set as 10) was drawn across from the anterior part to the posterior part (Fig. S1a). The signal intensities along the width of the line were measured and imported into R for generating intensity plots."

1. Figure 3d: Present a plot with the expected expression profiles of the three genes if the embryo is aligned as anticipated.

Response: We thank the reviewer for this helpful suggestion, which improves the clarity of our manuscript. We have added the following subfigure in as Figure 3d (Fig. 5) to show the expected expression profiles of the three midline genes along left-right axis.

See response letter for the figure.

1. Analysis Without Palette: Between lines 277-438, the outcome of using Palette with bulk RNA-seq and Stereo-Seq is convincing. However, consider the following:

o What would be the observations if the analysis were conducted solely with Stereo-Seq data, without incorporating bulk RNA-seq data and employing Palette?

Response: We thank the reviewer for raising this important question. Here we show the comparison of ST expression on stacked Stereo-seq slices, ST expression projected on 3D live images, and the Palette-inferred expression (Fig. 6). The stacked ST slices do not fully reflect the zebrafish morphology, and the gene expression appears sparse, making it look massive (the first row). While after projecting ST expression onto the live image, the expression patterns can be observed on zebrafish morphology, but the expression is still sparsely distributed in spots (the second row). However, the expression patterns captured by Palette in zSTEP show more continuous expression patterns (the third row), which are more similar to the observations in in situ hybridization images (the fourth row). We are considering put these analyses into the supplementary figure.

See response letter for the figure.

o This study uses only Stereo-Seq as the spatial transcriptomics reference. It would strengthen the argument to use at least one other spatial transcriptomics method, such as Visium or MERFISH, in conjunction with bulk RNA-seq and Palette, to demonstrate whether Palette consistently improves gene expression resolution.

Response: We thank the reviewer for raising this professional question. To demonstrate a broad application of Palette, it would be necessary to test Palette performance using different types of ST references. We plan to perform extra analyses to evaluate Palette performance using Visium and MERFISH data as ST references, respectively. Additionally, our Palette pipeline only takes the overlapped genes for inference. As only hundreds of genes can be detected by MERFISH, Palette can only infer the expression patterns of these genes. As mentioned in the work of Liu et al. (2023), MERFISH can independently resolve distinct cell types and spatial structures, and thus we believe Palette will also show great performance when using MERFISH as ST reference. We've already started the analyses and expect to accomplish it within the next month. And we will update the analyses as separated tutorials to the GitHub repository.

Reference:

Liu, J. et al. Concordance of MERFISH spatial transcriptomics with bulk and single-cell RNA sequencing. Life Sci Alliance 6 (2023).

1. PDAC Data Analysis: Provide a more detailed explanation of the PDAC data analysis and use appropriate colors in the tissue images to clearly distinguish cell types.

Response: We thank the reviewer for the suggestions. We have updated the colours used in the tissue images to be consistent to the colours in tissue clustering analysis. Additionally, we have added an additional subfigure in supplementary figure (Fig. 7) with more explanatory texts in the figure legends to provide a more thorough explanation for the analysis.

See response letter for the figure.

1. Comparison with Other Methods: State the limitations of not using STitch3D and Spateo for alignment and explain why these methods were not employed.

Response: We thank the reviewer for raising this constructive comment. We fully agree with you that the introduction of published alignment algorithms would be helpful in our analysis. Currently, the slice alignment is adjusted manually, and thus the main limitation of not using these tools is that manual operation may induce bias compared to the alignment generated by computational algorithm. Unfortunately, STitch3D and Spateo are not included in this study because of two reasons. First, these two newly developed tools have been recently posted, and our analyses were largely completed before that. Therefore, we only mentioned these tools in the Discussion section. Second, we do not want to embed too many external tools into our analysis, which may increase the difficulties for researchers' operation. Specifically, STitch3D and Spateo are configured to run in Python environment, while Palette is based on R packages. Moreover, without these tools, our current manual alignment also achieves desired performance. However, we value this enlightening suggestion by the reviewer and therefore plan to further compare the performance of manual alignment versus the mentioned two alignment tools. At present, we have a preliminary comparison scheme and collected relevant datasets. Hopefully, we will complete this analysis within the next 1 to 2 weeks.

Minor Comments:

1. References: Add references to the statements in lines 51-53.

Response: We thank the reviewer for reminding us of the missing references. We have added the works of Junker et al. (2014), Liu et al. (2022), Chen et al. (2022), Wang et al. (2022), Shi et al. (2023) and Satija et al. (2015) as references in line 53 as follows.

"Thus, great efforts are ongoing to construct gene expression maps of these models with higher resolution, depth, and comprehensiveness1-6."

References:

1. Junker, J.P. et al. Genome-wide RNA Tomography in the zebrafish embryo. Cell 159, 662-675 (2014).
2. Liu, C. et al. Spatiotemporal mapping of gene expression landscapes and developmental trajectories during zebrafish embryogenesis. Dev Cell 57, 1284-1298 e1285 (2022).
3. Chen, A. et al. Spatiotemporal transcriptomic atlas of mouse organogenesis using DNA nanoball-patterned arrays. Cell 185, 1777-1792 e1721 (2022).
4. Wang, M. et al. High-resolution 3D spatiotemporal transcriptomic maps of developing Drosophila embryos and larvae. Dev Cell 57, 1271-1283 e1274 (2022).
5. Shi, H. et al. Spatial atlas of the mouse central nervous system at molecular resolution. Nature 622, 552-561 (2023).
6. Satija, R. et al. Spatial reconstruction of single-cell gene expression data. Nature biotechnology 33, 495-502 (2015)

1. Scientific Name Consistency: Ensure consistency in using either "Danio rerio" or "zebrafish" throughout the manuscript.

Response: We thank the reviewer for this suggestion. We have changed "Danio rerio" to "zebrafish" to make "zebrafish" consistent throughout the manuscript.

1. Related References: Include the following relevant references:

o https://academic.oup.com/bib/article/25/4/bbae316/7705532

o https://www.life-science-alliance.org/content/6/1/e202201701

Response: We thank the reviewer for bringing these two relevant works to us. Baul et al. (2024) presented STGAT leveraging Graph Attention Networks for integrating spatial transcriptomics and bulk RNA-seq, and Liu et al. (2023) demonstrated the concordance of MERFISH ST with bulk and single-cell RNA-seq. Both are excellent works and relevant to our work. We have added these two references in line 61 and line 68, respectively.

References:

Baul, S. et al. Integrating spatial transcriptomics and bulk RNA-seq: predicting gene expression with enhanced resolution through graph attention networks. Brief Bioinform 25 (2024).

Liu, J. et al. Concordance of MERFISH spatial transcriptomics with bulk and single-cell RNA sequencing. Life Sci Alliance 6 (2023).

1. Figure 1a: In the Venn diagram, include the number of genes in the bulk and Stereo-Seq datasets, as well as the number of overlapping genes.

Response: We thank the reviewer reminding us to include these important numbers. And in our current manuscript, we have added the following sentences in the Methods section to provide the gene numbers (Fig. 8). While the Venn diagram in Figure 1a serves as a schematic representation, so we did not include the gene numbers, as these may vary depending on the actual data.

"Palette was performed on the aligned slices using the overlapped genes. For the 10 hpf embryo, there were 24,658 genes in the bulk data, 18,698 genes in the Stereo-seq data, and 16,601 overlapped genes. For the 12 hpf embryo, there were 23,018 genes in the bulk data, 18,948 genes in the Stereo-seq data, and 16,401 overlapped genes. For the 16 hpf embryo, there were 24,357 genes in the bulk data, 23,110 genes in the Stereo-seq data, and 19,539 overlapped genes."

See response letter for the figure.

1. Figure 1 Improvement: Enlarge Figure 1 and reduce repetitive elements, such as parts of the deconvolution and Figure 1b.

Response: We thank the reviewer for the helpful suggestion. We agree with the reviewer that the deconvolution sections appear repetitive. We have updated Figure 1 (Fig. 9) by replacing these repetitive elements with a clearer and simpler diagram.

See response letter for the figure.

1. Figure 3f: Explain the black discontinuous line in the plot.

Response: We thank the reviewer for the reminder. We are sorry about the lack of the explanation. We have added the below explanation for the black discontinuous line in the legend of Figure 3 (Fig. 10) as follows.

See response letter for the figure.

1. Line 610: State the percentage of unpaired imaging spots.

Response: We thank the review for the reminder. We are sorry about not including the paired and unpaired spot number. We have added the number of paired spots with the percentage in the total spots in the Method section as follows.

"The numbers of mapped spots for the 10 hpf, 12 hpf and 16 hpf embryos are 15,379 (69.4% of the total spots), 14,697 (70.5% of the total spots) and 21,605 (77.2% of the total spots), respectively."

1. Lines 616-618: Specify the unit for the spot diameter.

Response: We thank the reviewer for the reminder. Again, we are sorry about not including the spot diameter information in our previous version of manuscript. We have added the spot diameter in Method section as follows.

"In the Stereo-seq data, each spot contained 15 × 15 DNA nanoball (DNB) spots (The diameter of each spot is near 10 μm)."

Reviewer #1 (Significance):

This algorithm will be useful not only for the field of developmental biology but also for wider applications in spatial omics. Although I have expertise in spatial omics technology development, my understanding of computational biology is limited, which restricts my ability to fully evaluate the Palette algorithm presented in this paper.

Response: We thank the reviewer for recognizing our work, and we greatly appreciate the constructive suggestions from the reviewer. Although the reviewer acknowledged limited expertise in computational biology, the comments from the reviewer are highly professional and valuable. Following the suggestions from the reviewer, we have not only included more explanatory texts and figures to make the analysis procedures clearer and more understandable, but also supplemented the important parameters that were missing in our previous manuscript. We also provided extra figure to demonstrate the improvements of zSTEP on gene expression patterns. We believe that our work is now more scientific and more understandable, and we will continue working to solve the remaining issues as planned. We express our thanks for the reviewer again.

Reviewer #2 (Evidence, reproducibility and clarity):

The authors of the study introduce the Palette method, a novel approach designed to infer spatial gene expression patterns from bulk RNA-sequencing (RNA-seq) data. This method is complemented by the development of the DreSTEP 3D spatial gene expression atlas of zebrafish embryos, establishing a comprehensive resource for visualizing gene expression and investigating spatial cell-cell interactions in developmental biology.

Response: We sincerely appreciate the reviewer's positive feedback on our Palette pipeline and the zSTEP 3D spatial expression atlas of zebrafish embryos. We also thank the reviewer for the professional comments and constructive suggestions. The reviewer raised the concerns from the aspect of algorithm design and computational biology, which we did not address well in our previous manuscript. We agree with the reviewer that we did not clarify the selection criteria of the parameters in detail, and we are now working on the additional analyses to address this issue.

We also agree with the reviewer that we did not provide enough discussion of the strategies used in the pipeline, the features of Palette and the application scenarios of Palette and zSTEP. For wide use of our tools, it is significantly important to state these aspects. In this revised version, we have added more paragraphs in the Discussion section to address this issue. Additionally, we acknowledge that we did not adequately demonstrate the computational efficacy and computational requirements, which are important for researchers. We are also working on the additional analyses to address this issue.

Finally, we thank the reviewer again for the professional and constructive suggestions. These suggestions are addressable, and by following them, we believe our manuscript will see a significant improvement, especially in the Palette pipeline part, making the pipeline more rigorous and easier to access. We are confident that we can complete the planned additional tasks within the next 1-2 months.

1. The efficacy of the Palette method may be compromised by its dependency on the quality of the reference spatial transcriptomics data. As highlighted in the study, variations in data quality can lead to significant challenges in reconstructing accurate spatial expression patterns from bulk data. This underscores the necessity of evaluating quality parameters, such as the number of gene detections and spatial resolution, to ensure reliable outcomes. Additional studies should rigorously assess how these quality factors influence the accuracy and efficiency of the algorithm in various data contexts, particularly under diverse conditions of gene detection.

Response: We thank the reviewer for this valuable suggestion. We agree with the reviewer that the quality of the reference ST data may greatly influence the performance and efficacy of the Palette, and we have added paragraphs in the Discussion section to further discuss the impact of ST data quality on Palette performance. As mentioned by the reviewer, gene detections and spatial resolution are two important parameters that can influence the Palette performance. Low gene detection may impact the clustering process, making the cell types of spots not distinguished well. To evaluate the performance of Palette when ST data shows low gene detection, we plan to applied Palette using MERFISH data as the ST reference, which only captures hundreds of genes. Moreover, we will also investigate the impact of spatial resolution on Palette performance by merging ST spots to simulate lower resolution scenarios, as well as the impact of gene detection by randomly reducing detected genes. Through the comparison among the inferred expression patterns with ST data of different spatial resolutions or different numbers of detected genes, we can better access the performance of Palette and provide guidance to researchers on the appropriate ST data requirements for optimal performance. These analyses will take another one month to accomplish after this round of revision due to the limited response time.

1. The methodology raises pertinent questions regarding how the clustering results from different algorithms may affect the reconstructions by the Palette method. The authors would better provide a detailed discussion/comparison of clustering processes that optimize the reconstruction of spatial patterns, ensuring precision in the downstream analyses.

Response: We thank the reviewer for the constructive comments. We agree with the reviewer that the differences in clustering results would impact the inference of the Palette. In our Palette pipeline, rather than develop a new methodology for clustering, we employ the BayesSpace for spot clustering, which considers both spot transcriptional similarity and neighbouring structure for clustering. In this case, researchers may adjust the parameters in the BayesSpace package to achieve optimal clustering results. Actually, in most cases, the spot identities were achieved through UMAP analysis, which only considers the transcriptional differences but does not consider the spatial information. This kind of clustering strategy will potentially lead to an intricate arrangement of spots belonging to different clusters, and may result in sparse gene expression in Palette outcome, which is different from the patterns in bona fide tissues. Therefore, a suitable clustering strategy will definitely help capture the local patterns.

Moreover, our Palette pipeline also can use the clustering results from the tissue histomorphology. Using tissue histomorphology for clustering would be a good choice, as it is closer to the real case. The following Figure (Fig. 11) displays the Palette performance on PDAC datasets using both spatial clustering and histomorphology clustering strategies. The result using histomorphology clustering captures the weak pattern (indicated by the red circle) that were missed when using the spatial clustering (Fig. 11d).

See response letter for the figure.

1. The choice to utilize only highly expressed genes in the initial stages of the Palette algorithm also warrants further exploration. Addressing the criteria for determining which genes qualify as "highly expressed" and outlining robust cutoff will enhance the algorithm's rigor and applicability. Similarly, in the iterative estimation of gene expression across spatial spots, establishing optimal iteration conditions is crucial. Implementing a loss function may offer a systematic method for concluding iterations, thus refining computational efficiency.

Response: We thank the reviewer for the professional suggestions. As pointed out by the reviewer, the selection of highly expressed genes and the iteration times are two important parameters in our pipeline. The definition of highly expressed genes and the number of highly expressed genes are important for achieving a satisfactory clustering performance. We tested the impact of different numbers of highly expressed genes on cluster performance in our preliminary analyses, while we did not summarize these tests and specify the parameters. Therefore, we plan to include a supplementary figure showing the clustering performances under different definitions of highly expressed genes and different numbers of highly expressed genes. Additionally, for the iteration conditions, we have tested different iteration numbers to find out a suitable iteration number to achieve a stable expression in each spot. The following figure (Fig. 1) shows the results after performing Palette with different iteration times. We randomly selected 20 cells and compared their expression across tests with varying iteration times. The results indicate that for a ST dataset with 819 spots, the expression in each spot becomes nearly stable after 5000 iteration times. We previously did not consider the computational efficiency, while here the reviewer raises a valuable and professional suggestion to implement a loss function to determine the optimal number of iterations. We greatly appreciate this suggestion, and plan to apply a loss function to summarize the optimal iteration times for ST datasets of different sizes. This will provide guidance for potential researchers in selecting iteration times and enhance computational efficiency.

See response letter for the figure.

1. Performance metrics relating to processing speed and computational demands remain inadequately addressed in the current framework. Understanding how the Palette method scales across varying gene counts and bulk RNA-seq datasets will be essential for potential applications in larger biological contexts. Notably, the quantitative demands of analyzing 20,000 genes when processing 10, 100, or 1,000 bulk RNA profiles must be articulated to guide researchers in planning accordingly.

Response: We thank the reviewer for this valuable and professional suggestion. In our previous analyses, we did not consider the computation efficiency, processing speed and computational demands, which are important information for potential researchers. To address this issue, we will list our computer configuration first. And under this configuration, we plan to run Palette on datasets with different numbers of overlapped genes or ST references with varying spot numbers, and then summarize the running times into a metrics table. This will help researchers estimate the running time for their datasets and guide them in planning the analyses. We will begin the analyses soon and expect to complete the analysis within the next 1 to 2 months.

Minor opinions:

1. Despite the promising advances offered by the zebrafish 3D reconstruction, there is a lack of details regarding numbers of the spatial transcriptomics (ST) data utilized, and the number of bulk RNA-seq data employed in the analyses. These parameters need to be clarified.

Response: We thank the reviewer for reminding us of these parameters. We are sorry for not including these parameters in our previous manuscript. We have now included the numbers of bulk, ST and overlap genes in the Methods section as follows (Fig. 12).

"Palette was performed on the aligned slices using the overlapped genes. For the 10 hpf embryo, there were 24,658 genes in the bulk data, 18,698 genes in the Stereo-seq data, and 16,601 overlapped genes. For the 12 hpf embryo, there were 23,018 genes in the bulk data, 18,948 genes in the Stereo-seq data, and 16,401 overlapped genes. For the 16 hpf embryo, there were 24,357 genes in the bulk data, 23,110 genes in the Stereo-seq data, and 19,539 overlapped genes."

See response letter for the figure.

1. Issues regarding spatial cell-cell communication, especially concerning interactions over longer distances, necessitate careful consideration. Introducing spatial distance constraints could help formulate more realistic models of cellular interactions, a vital aspect of embryonic development.

Response: We thank the reviewer for this essential comment. We agree with the reviewer that the spatial distance is an essential factor to investigate in vivo cell-cell communication during embryonic development. Therefore, in our analyses, we employed CellChat for spatial cell-cell communication analysis, which can be used to infer and visualize spatial cell-cell communication network for ST datasets, considering the spatial distance as constrains of the computed communication probability. However, during our analyses, we observed that there were interactions between cell types over longer distances, as mentioned by the reviewer. We then investigated how these interactions of longer distances occurred. Here, we show the FGF interaction between tail bud and neural crest cells from our spatial cell-cell analysis as an example, and the distance between these two cell types appears quite significant (Fig. 13). We labelled tail bud cells and neural crest cells on the selected midline section and observed that, although most neural crest cells are distributed anteriorly, a small number of neural crest cells are located at tail, close to the tail bud cells. Therefore, the observed interaction between tail bud and neural crest cells is likely due to their adjacent distribution in the tail region, while the anteriorly distributed of neural crest spot in spatial cell-cell communication analysis reflects the anterior positioning of most neural crest cells. As a result, the distances shown on the spatial cell-cell communication analysis are not the real distance between two cell types.

In most cases in our spatial cell-cell communication analyses, the observed interactions over longer distances are likely influenced by this visualization strategy. Additionally, pre-processing the dataset may enhance the performance of the analyses. Here we performed systematic analyses of the entire embryo, which can make the interactions between cell types appear massive. To investigate specific biological questions, researchers can subset cell types of interest or categorize them into different subtypes based on their positions.

See response letter for the figure.

1. Evaluation metrics such as the Adjusted Rand Index (ARI) and Root Mean Square Error (RMSE) represent critical tools for systematically measuring the similarity of inferred spatial patterns, yet their specific application within this context should be elaborated.

Response: We thank the reviewer for recommending these two tools. We have applied them to evaluate the similarity between the expression patterns (Fig. 14). The inclusion of these statistical values makes our comparisons of expression patterns more scientific and convincing. And we have added the following texts in the Methods section to describe the calculation of these two values.

"The Adjusted Rand Index (ARI) and Root Mean Square Error (RMSE) were used to evaluate the similarity of the expression patterns. The expression patterns of in situ hybridization images were considered as the expected values, and the expression patterns of ST data and inferred expression patterns were compared to the expected values. Common positions along the AP axis within all three expression profiles were used, and the RMSE were calculated based on the scaled intensity of these positions. Values greater than the threshold were set to 1; otherwise, they were set to 0, and the ARI was then calculated based on the intensity category. Higher ARI and lower RMSE indicate greater similarity."

See response letter for the figure.

1. The study's limitations surrounding ST data quality cannot be overstated. Discussing scenarios where only limited or poor-quality ST data are available will be crucial for guiding future studies. Furthermore, a clear explanation of how enhanced specificity and accuracy translate into tangible biological insights is essential for demystifying the underlying mechanisms driving developmental processes.

Response: We thank the reviewer for raising this essential suggestion. We have realized that in our previous manuscript, our discussion on the advantages and limitations of Palette and zSTEP was neither broad nor detailed enough.

Therefore, in our revised manuscript, we have added the following paragraphs to further discuss the advantages and limitations of Palette and zSTEP, as well as the potential application of zSTEP in developmental biology.

In this section, we have emphasized again the impact of ST data quality on the performance of Palette and zSTEP, and then compared Palette with the strategy that uses well-established marker genes to infer spatial information. We demonstrated that although Palette cannot achieve single cell resolution, it captures the major expression patterns, which are closely correlated to biological functions and critical for embryonic development. Furthermore, we further discussed that zSTEP is not only a valuable tool for investigating gene expression patterns, but also has the potential in evaluating the reaction-diffusion model to investigate the complicated and well-choreographed pattern formation during embryonic development.

As here we have provided a more comprehensive discussion about Palette and zSTEP, we think that the potential researchers will better understand the application scenarios of our inference pipeline and our datasets. We hope our study can assist and inspire further research in the field of spatial transcriptomics and developmental biology.

"Thirdly, the performance of Palette and zSTEP heavily relied on the quality of ST data. If the quality of ST data is not of sufficient quality, the low-expression genes may not be detected or only appear in very few scattered spots, and the performance of spot clustering could also be affected. Moreover, in this study, for example, the Stereo-seq data of 12 hpf zebrafish embryo had fewer slices on the right side (Fig. S3b), resulting in more blank spots in the right part of zSTEP for the 12 hpf embryo. However, with the ongoing advancements in spatial resolution and data quality, the performance of Palette is expected to be enhanced and demonstrate even greater potential for analysing spatiotemporal gene expression.

On the other hand, compared to the brilliant strategy that infers spatial information of scRNA-seq data from well-established genes, our Palette pipeline cannot achieve single cell resolution. However, our Palette pipeline is based on the ST reference, and thus preserves the real positional relationships between spots. Furthermore, the focus of our pipeline is to infer the gene expression patterns, which are closely correlated to biological functions and critical for embryonic development, rather than the sparse expression within individual spots. In this regard, our Palette pipeline can be advantageous, as it allows for reconstruction of the major expression profiles, which are often more relevant for understanding developmental processes. Additionally, our Palette can be applied to serial sections, enabling the construction of 3D ST atlas.

Finally, while the current analyses demonstrated that zSTEP can serve as a valuable tool for identifying genes having specific patterns at certain developmental stages, the exploration of zSTEP is still limited. During animal development, pattern formation is always one of the most important developmental issues. As demonstrated by the reaction-diffusion (RD) model, morphogen molecules are produced at specific regions of the embryo, forming morphogen gradients to guide cell specification, while interactions between different morphogens instruct more complicated and well-choreographed pattern formation. Our Palette constructed zSTEP, as a comprehensive transcriptomic expression pattern during development, could be leveraged to evaluate and prove the RD model during development, including AP patterning. Moreover, the investigation of gene expression patterns should not be limited to morphogens and TFs, and further investigation of their roles in AP patterning is desirable. Additionally, here a random forest model may be sufficient for investigating the most essential morphogens and TFs for AP axis refinement, while more sophisticated machine learning models may be required for addressing more specific biological questions."

Reviewer #2 (Significance):

The Palette pipeline demonstrates a marked improvement in specificity and accuracy when predicting spatial gene expression patterns. Evaluative studies on Drosophila and zebrafish datasets affirm its enhanced performance compared to existing methodologies. By effectively reconstructing spatial information from bulk transcriptomic data, the Palette method innovatively merges the philosophy of leveraging single-cell transcriptomic data for deconvolution analyses. This integration is pivotal, advancing traditional bulk RNA-seq approaches while laying the groundwork for future research.

One of the notable achievements in this work is the construction of the DreSTEP atlas, which integrates serial bulk RNA-seq data with advanced 3D imaging techniques. This resource grants researchers unprecedented access to the visualization of gene expression patterns across the zebrafish embryo, facilitating the investigation of spatial relationships and cell-cell interactions critical for developmental processes. Such capabilities are invaluable for understanding the intricate dynamics of embryogenesis and the distinct roles of individual cell types.

Response: We thank the reviewer for the positive evaluation of our work, either the Palette pipeline or zSTEP. The reviewer has strong expertise in algorithm development and computational biology, and the concerns and suggestions from the reviewer are significantly precious and valuable for us. Regarding the bioinformatics tool development, we did not have extensive experiences, and thus we did not thoroughly address the selection criteria or clarify the parameters used in the pipeline, which may influence the application by other researchers. Therefore, we sincerely appreciate the professional suggestions from the reviewer, which we can follow to address these issues, improve our manuscript and make our work more impactful for researchers. Additionally, we did not consider computation efficiency, processing speed and computational demands, which would be important factors for other researchers to use Palette. We would like to add extra analyses to address these aspects.

Currently, based on the suggestions from the reviewer, we have added extra texts discussing the clustering strategy in Palette pipeline, the advantages and limitations of Palette, and the potential application of zSTEP in developmental biology. We believe that readers will now have a clearer understanding of the performance of Palette and the application scenarios of both Palette and zSTEP. We have not fully addressed the comments raised by the reviewer yet, while we are working on the planned additional analyses and expect to complete all these tasks within the next 1-2 months. We sincerely thank the reviewer for the professional and valuable suggestions, which definitely improve our work and will make it accessible for a wide range of researchers.

Finally, through this review process, we have learned a lot about the important considerations and requirements when designing bioinformatics tools, and we benefit a lot from the thoughtful guidance. We express our thanks to the reviewer again for the guidance, and we will try our best to address the remaining issues to further improve our manuscript.

Reviewer #3 (Evidence, reproducibility and clarity):

Evidence, reproducibility and clarity

In this study, Dong and colleagues developed a computational pipeline to use spatial transcriptomics (ST) datasets as a reference to infer the spatial patterns of gene expression from bulk RNA sequencing data. This approach aims to overcome the low read depth and limited gene detection capabilities in current ST datasets, while exploiting its ability to provide highly resolved spatial information. By combining bulk RNA-seq datasets from 3 developmental stages during early zebrafish development with previously available ST and imaging datasets, the authors build DreSTEP (Danio rerio spatiotemporal expression profiles). Using this approach, they go on to identify the morphogens and transcription factors involved in anteroposterior patterning.

The paper is well written, and the pipeline presented in this study is likely to be useful beyond the case studies included in this study. There are a few questions that, in my view, would be important to clarify to increase the impact of this work:

Response: We sincerely appreciate the positive feedback from the reviewer on the Palette pipeline and zebrafish spatiotemporal expression profiles zSTEP. We thank the reviewer for the constructive suggestions, which have inspired us to think deeply about application and advantages of Palette and zSTEP for future studies.

We fully agree with the reviewer that we do not sufficiently clarify the advantages and limitations of our inference pipeline in the original manuscript. The questions raised by the reviewer are very insightful. For example, while the inference expression patterns may closely resemble the in situ hybridization observation, which we consider as good performance, the reviewer pointed out that we should consider whether weak, yet real expression may have been removed. These questions have motivated us to think more deeply about the underlying principles and assumptions of our inference pipeline. Following the reviewer's questions, we have expanded our discussion on the application of zSTEP in developmental biology and the features of Palette compared to the existing strategies.

We believe that after incorporating the revisions, our current manuscript now demonstrates the application scenario of Palette clearer and suggested the application of zSTEP for investigating biological questions in developmental biology. We are grateful for the reviewer's guidance, which helps us increase the impact of our work.

1. The authors mention that they used a variable factor to adjust expression differences between the ST and bulk RNA-seq datasets. It would be important for the authors to comment on how much overlap in gene expression is necessary between the datasets for an accurate calculation of this variable factor? Can this be directly tested, for instance, by testing how their conclusions vary if expression is adjusted by a variable factor calculated from only a smaller set of genes?

Response: We thank the reviewer for the professional questions. We are sorry about not including the gene numbers in our previous manuscript. And now we have provided the numbers of genes in bulk and ST data and the numbers of the overlapped genes (Fig. 15).

"Palette was performed on the aligned slices using the overlapped genes. For the 10 hpf embryo, there were 24,658 genes in the bulk data, 18,698 genes in the Stereo-seq data, and 16,601 overlapped genes. For the 12 hpf embryo, there were 23,018 genes in the bulk data, 18,948 genes in the Stereo-seq data, and 16,401 overlapped genes. For the 16 hpf embryo, there were 24,357 genes in the bulk data, 23,110 genes in the Stereo-seq data, and 19,539 overlapped genes."

See response letter for the figure.

For Palette implementation, we took all the overlapped genes. To calculate the variable factor, we aggregated the expression of each gene in the ST data, and then used the expression of the bulk data to divide the aggregated expression for variable factor calculation. As a result, each overlapped gene was assigned a variable factor to adjust its expression, based on its difference between bulk and ST data. The rationale behind this approach is that by considering the ST data as a whole, we can effectively reduce the variations among individual spots. This allows the variable factors to provide reasonable adjustment to gene expression.

Above all, the variable factors can be directly calculated. Currently Palette only can infer the expression patterns of overlapped genes. It means when the number of overlapped genes is small, such as MERFISH only detecting hundreds of genes, Palette can only infer the expression patterns of these genes. However, if the MERFISH data have good quality, which enable resolving distinct cell types, we believe Palette will also show good performance when using MERFISH as ST reference. Additionally, we plan to perform Palette using MERFISH as ST reference to further demonstrate its broad application when using different ST references.

1. Palette gives rise to highly spatially precise patterns, which closely match those found in ISH. However, the smoothening of the expression can also remove weak, yet real, local expression patterns, as shown for idgf6 in Fig. 2a. Can the authors test this more extensively for other genes?

Response: We thank the reviewer for this essential question. We agree with the reviewer that weak, yet real expression might be removed in our Palette inference pipeline. The weak, sparse expression may be due to the ST technique itself or the variations in samples. However, that sparse gene expression may not have biological meaning, and the focus of our pipeline in to capture the expression patterns, which are closely correlated with functions and crucial for embryonic development. Therefore, our algorithm considers spot characteristics and emphasize cluster-specific expression, resulting in spatial-specific expression patterns. In most cases, the main gene expression patterns can be captured, which can help understand gene functions and roles in embryonic development. We have updated Supplementary Figure S1a (Fig. 16) to include more gene patterns to demonstrate this point.

See response letter for the figure.

1. Using adjacent slices for ST and "bulk RNA-seq" may provide better results than those obtained when comparing two independent datasets. Could the authors also extend the analysis of Palette's functionalities by using separate, previously available but independent datasets, for ST and bulk RNA-seq in Drosophila as well?

Response: We thank the reviewer for the valuable question. We agree with the reviewer that using adjacent slices may provide better results. The idea here is that the inferred spatial expression patterns from pseudo bulk RNA-seq can be used to compare with the real expression of ST to evaluate Palette performance. We have updated our Figure 2a (Fig. 17) to illustrate the analysis clearer.

See response letter for the figure.

To demonstrate the Palette's functionalities, we have used Palette to infer zebrafish bulk RNA-seq slice (Junker et al., 2014) using Stereo-seq slice (Liu et al., 2022) as ST reference, and these two datasets are separate and independent. We agree with the reviewer that it would be good to use separate datasets to test in Drosophila to further demonstrate the Palette's functionalities. However, unfortunately, we did not find the Drosophila serial bulk RNA-seq data along left-right axis of the corresponding stages, and thus we might be unable to perform the extra analyses using independent Drosophila datasets.

References:

Junker, J.P. et al. Genome-wide RNA Tomography in the zebrafish embryo. Cell 159, 662-675 (2014).

Liu, C. et al. Spatiotemporal mapping of gene expression landscapes and developmental trajectories during zebrafish embryogenesis. Dev Cell 57, 1284-1298 e1285 (2022).

1. The DreSTEP analysis in zebrafish embryos is interesting and validates well-established observations in the field. Can the authors also discuss whether and how their dataset allows them to refine our understanding of the spatial or temporal pattern of the morphogens and TFs involved in AP patterning? This would further validate their approach.

Response: We appreciate the reviewer for recognition of our zSTEP and raising this valuable question, which has inspired us to think more deeply about the potential application of zSTEP in developmental biology. As the reviewer noted, our zSTEP analyses have validated well-established observations in the field. Rather than focusing on the sparse expression detected in ST data, zSTEP emphasizes the gene expression patterns that are closely correlated with biological functions and critical for embryonic development. Therefore, zSTEP can serve as a valuable tool for identifying the genes having specific patterns at certain developmental stages.

Pattern formation is one of the most important developmental issues for all animals. The reaction-diffusion (RD) model is a widely recognized theoretical framework used to explain self-regulated pattern formation in developing animal embryos (Kondo & Miura, 2010). Morphogen molecules are produced at specific regions of the embryo, forming morphogen gradients to guide cell specification. Most importantly, interactions between different morphogens instruct more complicated and well-choreographed pattern formation. Our Palette-constructed zSTEP provides a comprehensive transcriptomic expression pattern, including all morphogens and TFs, across the whole embryo during development. These valuable resources, in our opinion, could be leveraged to evaluate and prove the RD model during development, including AP patterning. In our current zSTEP analyses, we have already identified genes that exhibit specific expression patterns along AP axis, some of which have not been fully characterized. These genes could be potential targets for further investigation into their roles in AP patterning, although they are not the primary focus of this study. Additionally, our analyses only focused on morphogens and TFs, but zSTEP can be used to investigate the expression patterns of other genes as well. Moreover, we employed a random forest model to investigate the most essential morphogens and TFs for AP axis refinement, which is one of the basic applications of zSTEP. To investigate specific biological questions of interest, it would be worth exploring the use of more sophisticated machine learning models.

We have added the following paragraph in the Discussion section to discuss the potential application of zSTEP in future studies.

"Finally, while the current analyses demonstrated that zSTEP can serve as a valuable tool for identifying genes having specific patterns at certain developmental stages, the exploration of zSTEP is still limited. During animal development, pattern formation is always one of the most important developmental issues. As demonstrated by the reaction-diffusion (RD) model, morphogen molecules are produced at specific regions of the embryo, forming morphogen gradients to guide cell specification, while interactions between different morphogens instruct more complicated and well-choreographed pattern formation. Our Palette constructed zSTEP, as a comprehensive transcriptomic expression pattern during development, could be leveraged to evaluate and prove the RD model during development, including AP patterning. Moreover, the investigation of gene expression patterns should not be limited to morphogens and TFs, and further investigation of their roles in AP patterning is desirable. Additionally, here a random forest model may be sufficient for investigating the most essential morphogens and TFs for AP axis refinement, while more sophisticated machine learning models may be required for addressing more specific biological questions."

Reference

Kondo, S. & Miura, T. Reaction-Diffusion model as a framework for understanding biological pattern formation. Science 329, 1616-1620 (2010).

1. Can the authors comment on the limits of this inference pipeline? And how it performs as compared to single-cell RNA sequencing datasets where spatial information is inferred from well-established marker genes?

Response: We appreciate the reviewer for this insightful question, which has inspired us to further explore the advantages and limitations of the Palette pipeline in comparison with other inference strategies. As mentioned in the Discussion section, a key limitation of the inference pipeline is its heavy reliance on the quality of ST data. It is obvious that if the quality of ST data is not of sufficient quality, the low-expression genes may not be detected or only appear in very few scattered spots. We think it is a common issue for any inference tools using ST data as the reference. However, with the ongoing advancements in spatial resolution and data quality, the performance of Palette is expected to be improved.

As a comparison, the single-cell RNA sequencing datasets where spatial information is inferred from well-established marker genes do not face this limitation. The ground-breaking work by Satija et al. (2015) used such a strategy that combined scRNA-seq and in situ hybridizations of well-established marker genes to infer spatial location, enabling single cell resolution, as it maintains the high read depth and gene detection. One advantages of this scRNA-seq-based strategy is that it provides the transcriptomics of individual cells, rather than a combination of cell within a ST spot, although the positional relationships between cells are not real.

However, compared to the inference from ST data, the positional relationships between cells are not directly captured. On the other hand, as the embryonic development progresses, more cell types will be specified, and the body patterning becomes more complex. In this scenario, using well-established marker gene to infer spatial information would be much more challenging. Additionally, there are not many scRNA-seq datasets of serial sections, and thus this strategy may not be used to construct 3D ST atlas.

In contrast, our Palette inference pipeline is based on the ST data, which preserves the real positional relationships between spots. Although our inference pipeline cannot achieve single cell resolution, it focuses on the gene expression patterns rather than the sparse expression within individual spots. By applying Palette to paired serial sections, we were able to generated a 3D spatial expression atlas of zebrafish embryos, which has showed promising performance for investigating gene expression patterns and their involvement in AP patterning.

Reference

Satija, R. et al. Spatial reconstruction of single-cell gene expression data. Nature biotechnology 33, 495-502 (2015)

We have updated the following paragraphs to further demonstrating the limitation of the inference pipeline in details in the Discussion section.

"Thirdly, the performance of Palette and zSTEP heavily relied on the quality of ST data. If the quality of ST data is not of sufficient quality, the low-expression genes may not be detected or only appear in very few scattered spots, and the performance of spot clustering could also be affected. Moreover, in this study, for example, the Stereo-seq data of 12 hpf zebrafish embryo had fewer slices on the right side (Fig. S3b), resulting in more blank spots in the right part of zSTEP for the 12 hpf embryo. However, with the ongoing advancements in spatial resolution and data quality, the performance of Palette is expected to be enhanced and demonstrate even greater potential for analysing spatiotemporal gene expression.

On the other hand, compared to the brilliant strategy that infers spatial information of scRNA-seq data from well-established genes, our Palette pipeline cannot achieve single cell resolution. However, our Palette pipeline is based on the ST reference, and thus preserves the real positional relationships between spots. Furthermore, the focus of our pipeline is to infer the gene expression patterns, which are closely correlated to biological functions and critical for embryonic development, rather than the sparse expression within individual spots. In this regard, our Palette pipeline can be advantageous, as it allows for reconstruction of the major expression profiles, which are often more relevant for understanding developmental processes. Additionally, our Palette can be applied to serial sections, enabling the construction of 3D ST atlas."

Reviewer #3 (Significance):

This study tackles an important challenge in biology - the difficult to resolve gene expression patterns with high spatial precision and in a high-throughput manner. By integrating sequencing datasets from previously published studies, as well as newly-generated datasets, the authors provide evidence that their novel inference pipeline enables them to obtain high-quality spatial information simply from bulk RNA-seq datasets, using ST as a reference. The development of this pipeline - Palette - is a major part of this manuscript and its applicability is validated using datasets from Drosophila and zebrafish embryos. This in an important advance for the field, but it would be nice for the authors to further comment on i) the validity of some of their approaches and how they may influence the quality of their inference, as well as, ii) potential pitfalls/limitations of this approach as compared to others available in the field. This would synthetize both previous and current findings into a conceptual and technological framework that would have a strong impact well beyond cell and developmental biology.

Audience: This study would be relevant for a broad audience of biologists, interested in morphogen signaling, gene regulatory networks and cell fate specification.

Expertise in zebrafish development, gastrulation, morphogen signaling and morphogenesis.

Response: We thank the reviewer for providing the positive feedback, arising these valuable questions, which have motivated us to deeply consider the design concept and further application of Palette and zSTEP. Based on the insightful questions from the reviewer, we have added two extra paragraphs in the Discussion section to further discuss the potential application of zSTEP in developmental biology and application scenarios of the Palette pipeline. Specially, we have demonstrated that the performance of the inference pipeline relies on the spatial resolution and data quality of the ST data. We have then compared the advantages and limitations of Palette with the existing brilliant spatial inference strategy, which infers spatial information of scRNA-seq from well-established marker genes. Although our inference pipeline cannot achieve single cell resolution, it can capture the major expression patterns, which are closely correlated to functions and critical for embryonic development. We believe this will help readers gain a clearer understanding of the advantage and limitations of our pipeline compared to other tools, as well as the tasks for which Palette and our constructed zSTEP can be utilized. We express our thanks to the reviewer again for the valuable comments.

Author response:

The following is the authors’ response to the current reviews.

We would like to thank the reviewers for their efforts and feedback on our preprint. We have elected to rework the manuscript for publication in a different journal. In this process we will alter many of the approaches and re-evaluate the conclusions. With this, many of the points raised by the reviewers will be no longer relevant and therefore do not require a response. Again, we thank the reviewers for their time and helpful feedback.

The following is the authors’ response to the original reviews.

eLife Assessment:

The authors present a potentially useful approach of broad interest arguing that anterior cingulate cortex (ACC) tracks option values in decisions involving delayed rewards. The authors introduce the idea of a resource-based cognitive effort signal in ACC ensembles and link ACC theta oscillations to a resistance-based strategy. The evidence supporting these new ideas is incomplete and would benefit from additional detail and more rigorous analyses and computational methods.

We are extremely grateful for the several excellent and comments of the reviewers. To address these concerns, we have completely reworked the manuscript adding more rigorous approaches in each phase of the analysis and computational model. We realize that this has taken some time to prepare the revision. However, given the comments of the reviewers, we felt it necessary to thoroughly rework the paper based on their input. Here is a (nonexhaustive) overview of the major changes we made:

We have developed a way to more adequately capture the heterogeneity in the behavior

We have completely reworked the RL model

We have added additional approaches and rigor to the analysis of the value-tracking signal. 

Reviewer #1 (Public Review):

Summary:

Young (2.5 mo [adolescent]) rats were tasked to either press one lever for immediate reward or another for delayed reward. 

Please note that at the time of testing and training that the rats were > 4 months old. 

The task had a complex structure in which (1) the number of pellets provided on the immediate reward lever changed as a function of the decisions made, (2) rats were prevented from pressing the same lever three times in a row. Importantly, this task is very different from most intertemporal choice tasks which adjust delay (to the delayed lever), whereas this task held the delay constant and adjusted the number of 20 mg sucrose pellets provided on the immediate value lever.

Several studies parametrically vary the immediate lever (PMID: 39119916, 31654652, 28000083, 26779747, 12270518, 19389183). While most versions of the task will yield qualitatively similar estimates of discounting, the adjusting amount is preferred as it provides the most consistent estimates (PMID: 22445576). More specifically this version of the task avoids contrast effects of that result from changing the delay during the session (PMID: 23963529, 24780379, 19730365, 35661751) which complicates value estimates. 

Analyses are based on separating sessions into groups, but group membership includes arbitrary requirements and many sessions have been dropped from the analyses. 

We have updated this approach and now provide a more comprehensive assessment of the behavior. The updated approach applies a hierarchical clustering model to the behavior in each session. This was applied at each delay to separate animals that prefer the immediate option more/less. This results in 4 statistically dissociable groups (4LO, 4HI, 8LO, 8HI) and includes all sessions. Please see Figure 1. 

Computational modeling is based on an overly simple reinforcement learning model, as evidenced by fit parameters pegging to the extremes. 

We have completely reworked the simulations in the revision. In the updated RL model we carefully add parameters to determine which are necessary to explain the experimental data. We feel that it is simplified yet more descriptive. Please see Figure 2 and associated text. 

The neural analysis is overly complex and does not contain the necessary statistics to assess the validity of their claims.

We have dramatically streamlined the spike train analysis approach and added several statistical tests to ensure the rigor of our results. Please see Figures 4,5,6 and associated text. 

Strengths:

The task is interesting.

Thank you for the positive comment

Weaknesses:

Behavior:

The basic behavioral results from this task are not presented. For example, "each recording session consisted of 40 choice trials or 45 minutes". What was the distribution of choices over sessions? Did that change between rats? Did that change between delays? Were there any sequence effects? (I recommend looking at reaction times.) Were there any effects of pressing a lever twice vs after a forced trial? 

Please see the updated statistics and panels in Figures 1 and 2. We believe these address this valid concern.  

This task has a very complicated sequential structure that I think I would be hard pressed to follow if I were performing this task. 

Human tasks implement a similar task structure (PMID: 26779747). Please note the response above that outlines the benefits of using of this task.   

Before diving into the complex analyses assuming reinforcement learning paradigms or cognitive control, I would have liked to have understood the basic behaviors the rats were taking. For example, what was the typical rate of lever pressing? If the rats are pressing 40 times in 45 minutes, does waiting 8s make a large difference?

Thank you for this suggestion. Our additions to Figure 1 are intended to better explain and quantify the behavior of the animals. Note that this task is designed to hold the rate of reinforcement constant no matter the choices of the animals. Our analysis supports the long-held view in the literature that rats do not like waiting for rewards, even at small delays. Going from the 4 à 8 sec delay results in significantly more immediate choices, indicating that the rats will forgo waiting 8 sec for a larger reinforcer and take a smaller reinforcer at 4 sec.  

For that matter, the reaction time from lever appearance to lever pressing would be very interesting (and important). Are they making a choice as soon as the levers appear? Are they leaning towards the delay side, but then give in and choose the immediate lever? What are the reaction time hazard distributions?

This is an excellent suggestion, we have added a brief analysis of reaction times (Please see the section entitled “4 behavioral groups are observed across all sessions” in the Results). Please note that an analysis of the reaction times has been presented in a prior analysis of this data set (White et al., 2024). In addition, an analysis of reaction times in this task was performed in Linsenbardt et al. (2017). In short, animals tend to choose within 1 second of the lever appearing. In addition, our prior work shows that responses on the immediate lever tend to be slower, which we viewed as evidence of increased deliberation requirements (possibly required to integrate value signals).   

It is not clear that the animals on this task were actually using cognitive control strategies on this task. One cannot assume from the task that cognitive control is key. The authors only consider a very limited number of potential behaviors (an overly simple RL model). On this task, there are a lot of potential behavioral strategies: "win-stay/lose-shift", "perseveration", "alternation", even "random choices" should be considered.

The strategies the Reviewer mentioned are descriptors of the actual choices the rats made. For example, perseveration means the rat is choosing one of the levers at an excessively high rate whereas alternation means it is choosing the two levers more or less equally, independent of payouts. But the question we are interested in is why? We are arguing that the type of cognitive control determines the choice behavior, but cognitive control is an internal variable that guides behavior, rather than simply a descriptor of the behavior. For example, the animal opts to perseverate on the delayed lever because the cognitive control required to track ival is too high. We then searched the neural data for signatures of the two types of cognitive control.

The delay lever was assigned to the "non-preferred side". How did side bias affect the decisions made?

The side bias clearly does not impact performance as the animals prefer the delay lever at shorter delays, which works against this bias.  

The analyses based on "group" are unjustified. The authors compare the proportion of delayed to immediate lever press choices on the non-forced trials and then did k-means clustering on this distribution. But the distribution itself was not shown, so it is unclear whether the "groups" were actually different. They used k=3, but do not describe how this arbitrary number was chosen. (Is 3 the optimal number of clusters to describe this distribution?) Moreover, they removed three group 1 sessions with an 8s delay and two group 2 sessions with a 4s delay, making all the group 1 sessions 4s delay sessions and all group 2 sessions 8s delay sessions. They then ignore group 3 completely. These analyses seem arbitrary and unnecessarily complex. I think they need to analyze the data by delay. (How do rats handle 4s delay sessions? How do rats handle 6s delay sessions? How do rats handle 8s delay sessions?). If they decide to analyze the data by strategy, then they should identify specific strategies, model those strategies, and do model comparison to identify the best explanatory strategy. Importantly, the groups were session-based, not rat based, suggesting that rats used different strategies based on the delay to the delayed lever.

We have completely reworked our approach for capturing the heterogeneity in behavior. We have taken care to show more of the behavioral statistics that have gone into identifying each of the groups. All sessions are included in this analysis. As the reviewer suggests, we used the statistics from each of the behavioral groups to inform the RL model that explores neural signals that underly decisions in this task. We strongly disagree that groups should be rat and not session based as the behavior of the animal can, and does, change from day to day. This is important to consider when analyzing the neural data as rat-based groupings would ignore this potential source of variance. 

The reinforcement learning model used was overly simple. In particular, the RL model assumes that the subjects understand the task structure, but we know that even humans have trouble following complex task structures. Moreover, we know that rodent decision-making depends on much more complex strategies (model-based decisions, multi-state decisions, rate-based decisions, etc). There are lots of other ways to encode these decision variables, such as softmax with an inverse temperature rather than epsilon-greedy. The RL model was stated as a given and not justified. As one critical example, the RL model fit to the data assumed a constant exponential discounting function, but it is well-established that all animals, including rodents, use hyperbolic discounting in intertemporal choice tasks. Presumably this changes dramatically the effect of 4s and 8s. As evidence that the RL model is incomplete, the parameters found for the two groups were extreme. (Alpha=1 implies no history and only reacting to the most recent event. Epsilon=0.4 in an epsilongreedy algorithm is a 40% chance of responding randomly.)

While we agree that the approach was not fully justified, we do not agree that it was invalid. Simply stated, a softmax approach gives the best fit to the choice behavior, whereas our epsilon-greedy approach attempted to reproduce the choice behavior using a naïve agent that progressively learns the values of the two levers on a choice-by-choice basis. Nevertheless, we certainly appreciate that important insights can be gained by fitting a model to the data as suggested. We feel that the new modeling approach we have now implemented is optimal for the present purposes and it replaces the one used in the original manuscript.

The authors do add a "dbias" (which is a preference for the delayed lever) term to the RL model, but note that it has to be maximal in the 4s condition to reproduce group 2 behavior, which means they are not doing reinforcement learning anymore, just choosing the delayed lever.

The dbias term was dropped in the new model implementation

Neurophysiology:

The neurophysiology figures are unclear and mostly uninterpretable; they do not show variability, statistics or conclusive results.

While the reviewer is justified in criticizing the clarity of the figures, the statement that “they do not show variability, statistics or conclusive results” is not correct. Each of the figures presented in the first draft of the manuscript, except Figure 3, are accompanied by statistics and measures of variability. Nonetheless we have updated each of the neurophysiology analyses. We hope that the reviewer will find our updates more rigorous and thorough.   

As with the behavior, I would have liked to have seen more traditional neurophysiological analyses first. What do the cells respond to? How do the manifolds change aligned to the lever presses? Are those different between lever presses?

We have added several figures that plot the mean +/- SEM of the neural activity (see Figures 4 and 5). Hopefully this provides a more intuitive picture of the changes in neural activity throughout the task.  

Are there changes in cellular information (both at the individual and ensemble level) over time in the session? 

We provide several analyses of how firing rate changes over trials in relation to ival over time and trials in the session. In addition, we describe how these signals change in each of the behavioral groups. 

How do cellular responses differ during that delay while both levers are out, but the rats are not choosing the immediate lever?

We were somewhat unclear about this suggestion as the delay follows the lever press. In addition, there is no delay after immediate presses 

Figure 3, for example, claims that some of the principal components tracked the number of pellets on the immediate lever ("ival"), but they are just two curves. No statistics, controls, or justification for this is shown. BTW, on Figure 3, what is the event at 200s?

This comment is no longer relevant based on the changes we’ve made to the manuscript. 

I'm confused. On Figure 4, the number of trials seems to go up to 50, but in the methods, they say that rats received 40 trials or 45 minutes of experience.

This comment is no longer relevant based on the changes we’ve made to the manuscript. 

At the end of page 14, the authors state that the strength of the correlation did not differ by group and that this was "predicted" by the RL modeling, but this statement is nonsensical, given that the RL modeling did not fit the data well, depended on extreme values. Moreover, this claim is dependent on "not statistically detectable", which is, of course, not interpretable as "not different".

This comment is no longer relevant based on the changes we’ve made to the manuscript. 

There is an interesting result on page 16 that the increases in theta power were observed before a delayed lever press but not an immediate lever press, and then that the theta power declined after an immediate lever press. 

Thank you for the positive comment. 

These data are separated by session group (again group 1 is a subset of the 4s sessions, group 2 is a subset of the 8s sessions, and group 3 is ignored). I would much rather see these data analyzed by delay itself or by some sort of strategy fit across delays.

Thank you for the excellent suggestion. Our new group assignments take delay into account. 

That being said, I don't see how this description shows up in Figure 6. What does Figure 6 look like if you just separate the sessions by delay?

We are unclear what the reviewer means by “this description”.  

Discussion:

Finally, it is unclear to what extent this task actually gets at the questions originally laid out in the goals and returned to in the discussion. The idea of cognitive effort is interesting, but there is no data presented that this task is cognitive at all. The idea of a resourced cognitive effort and a resistance cognitive effort is interesting, but presumably the way one overcomes resistance is through resourcelimited components, so it is unclear that these two cognitive effort strategies are different.

The basis for the reviewers assertation that “the way one overcomes resistance is through resourcelimited components” is not clear. In the revised version, we have taken greater care to outline how each type of effort signal facilitates performance of the task and articulate these possibilities in our stochastic and RL models. We view the strong evidence for ival tracking presented herein as a critical component of resource based cognitive effort. 

The authors state that "ival-tracking" (neurons and ensembles that presumably track the number of pellets being delivered on the immediate lever - a fancy name for "expectations") "taps into a resourced-based form of cognitive effort", but no evidence is actually provided that keeping track of the expectation of reward on the immediate lever depends on attention or mnemonic resources. They also state that a "dLP-biased strategy" (waiting out the delay) is a "resistance-based form of cognitive effort" but no evidence is made that going to the delayed side takes effort.

We challenge the reviewers that assertation ival tracking is a “fancy name for expectations”. We make no claim about the prospective or retrospective nature of the signal. Clearly, expectations should be prospective and therefore different from ival tracking. Regarding the resistance signal: First, animals avoid the delay lever more often at the 8 sec delay (Figure 1). We have shown that increasing the delay systematically biases responses AWAY from the delay (Linsenbardt et al., 2017). This is consistent with a well-developed literature that rats and mice do not like waiting for delayed reinforcers. We contend that enduring something you don’t like takes effort. 

The authors talk about theta synchrony, but never actually measure theta synchrony, particularly across structures such as amygdala or ventral hippocampus. The authors try to connect this to "the unpleasantness of the delay", but provide no measures of pleasantness or unpleasantness. They have no evidence that waiting out an 8s delay is unpleasant.

We have added spike-field coherence to better contact the literature on synchrony. Note that we never refer to our results as “synchrony”. However, we would be remiss to not address the growing literature on theta synchrony in effort allocation. There is a well-developed literature that rats and mice do not like waiting for delayed reinforcers. If waiting out the delay was not pleasant then why do the animals forgo larger rewards to avoid it? 

The authors hypothesize that the "ival-tracking signal" (the expectation of number of pellets on the immediate lever) "could simply reflect the emotional or autonomic response". Aside from the fact that no evidence for this is provided, if this were to be true, then, in what sense would any of these signals be related to cognitive control?

This is proposed as an alternative explanation to the ival signal in the discussion. It was added as our due diligence. Emotional state could provide feedback to the currently implemented control mechanism. If waiting for reinforcement is too unpleasant this could drive them to ival tracking and choosing the immediate option more frequently. We provide this option only as a possibility, not a conclusion. We have clarified this in the revised text. Nevertheless, based on our review of the literature, autonomic tracking in some form, seems to be the most likely function of ACC (Seamans & Floresco 2022). While the reviewer may disagree with this, we feel it is at least as valid as all the complex, cognitively-based interpretations that commonly appear in the literature.

Reviewer #2 (Public Review):

Summary:

This manuscript explores the neuronal signals that underlie resistance vs resource-based models of cognitive effort. The authors use a delayed discounting task and computational models to explore these ideas. The authors find that the ACC strongly tracks value and time, which is consistent with prior work. Novel contributions include quantification of a resource-based control signal among ACC ensembles, and linking ACC theta oscillations to a resistance-based strategy.

Strengths:

The experiments and analyses are well done and have the potential to generate an elegant explanatory framework for ACC neuronal activity. The inclusion of local-field potential / spike-field analyses is particularly important because these can be measured in humans.

Thank you for the endorsement of our work.

Weaknesses:

I had questions that might help me understand the task and details of neuronal analyses.

(1) The abstract, discussion, and introduction set up an opposition between resource and resistancebased forms of cognitive effort. It's clear that the authors find evidence for each (ACC ensembles = resource, theta=resistance?) but I'm not sure where the data fall on this dichotomy.

(a) An overall very simple schematic early in the paper (prior to the MCML model? or even the behavior) may help illustrate the main point.

(b) In the intro, results, and discussion, it may help to relate each point to this dichotomy.

(c) What would resource-based signals look like? What would resistance based signals look like? Is the main point that resistance-based strategies dominate when delays are short, but resource-based strategies dominate when delays are long?

(d) I wonder if these strategies can be illustrated? Could these two measures (dLP vs ival tracking) be plotted on separate axes or extremes, and behavior, neuronal data, LFP, and spectral relationships be shown on these axes? I think Figure 2 is working towards this. Could these be shown for each delay length? This way, as the evidence from behavior, model, single neurons, ensembles, and theta is presented, it can be related to this framework, and the reader can organize the findings.

These are excellent suggestions, and we have implemented them, where possible. 

(2) The task is not clear to me.

(a) I wonder if a task schematic and a flow chart of training would help readers.

Yes, excellent idea, we have now included this in Figure 1. 

(b) This task appears to be relatively new. Has it been used before in rats (Oberlin and Grahame is a mouse study)? Some history / context might help orient readers.

Indeed, this task has been used in rats in several prior studies in rats. Please see the following references (PMID: 39119916, 31654652, 28000083, 26779747, 12270518, 19389183).

(c) How many total sessions were completed with ascending delays? Was there criteria for surgeries? How many total recording sessions per animal (of the 54?)

Please note that the delay does not change within a session. There were no criteria for surgery. 

(d) How many trials completed per session (40 trials OR 45 minutes)? Where are there errors? These details are important for interpreting Figure 1.

Every animal in this data set completed 40 trials and we have updated the task description to clarify this issue. There are no errors in this task, but rather the task is designed to the tendency to make an impulsive choice (smaller reward now). 

(3) Figure 1 is unclear to me.

(a) Delayed vs immediate lever presses are being plotted - but I am not sure what is red, and what is blue. I might suggest plotting each animal.

We have updated Figure 1 considerably for clarity. 

(b) How many animals and sessions go into each data point?

We hope this is clarified now with our new group assignments as all sessions were included in the analysis. 

(c) Table 1 (which might be better referenced in the paper) refers to rats by session. Is it true that some rats (2 and 8) were not analyzed for the bulk of the paper? Some rats appear to switch strategies, and some stay in one strategy. How many neurons come from each rat?

We have updated Table 1 based on our new groupings. The rats that contribute the most sessions also tend to be represented across the behavioral groups therefore it is unlikely that effort allocation strategies across groupings are an esoteric feature of an animal. 

(d) Task basics - RT, choice, accuracy, video stills - might help readers understand what is going into these plots

(e) Does the animal move differently (i.e., RTs) in G1 vs. G2?

Excellent suggestion. We have added more analysis of the task variables in the revision (e.g. RT, choice comparisons across delays, etc…)

(4) I wasn't sure how clustered G1 vs. G2 vs G3 are. To make this argument, the raw data (or some axis of it) might help.

(a) This is particularly important because G3 appears to be a mix of G1 and G2, although upon inspection, I'm not sure how different they really are

(b) Was there some objective clustering criteria that defined the clusters?

(c) Why discuss G3 at all? Can these sessions be removed from analysis?

Based on our updates to the behavioral analysis these comments are no longer relevant. 

(5) The same applies to neuronal analyses in Fig 3 and 4

(a) What does a single neuron peri-event raster look like? I would include several of these.

(b) What does PC1, 2 and 3 look like for G1, G2, and G3?

(c) Certain PCs are selected, but I'm not sure how they were selected - was there a criteria used? How was the correlation between PCA and ival selected? What about PCs that don't correlate with ival?

(d) If the authors are using PCA, then scree plots and PETHs might be useful, as well as comparisons to PCs from time-shuffled / randomized data.

We hope that our reworking of the neural data analysis has clarified these issues. We now include several firing rate examples and aggregate data.   

(6) I had questions about the spectral analysis

(a) Theta has many definitions - why did the authors use 6-12 Hz? Does it come from the hippocampal literature, and is this the best definition of theta? What about other bands (delta - 1-4 Hz), theta (4-7 Hz); and beta - 13- 30 Hz? These bands are of particular importance because they have been associated with errors, dopamine, and are abnormal in schizophrenia and Parkinson's disease.

This designation comes mainly from the hippocampal and ACC literature in rodents. In addition, this range best captured the peak in the power spectrum in our data. Note that we focus our analysis on theta give the literature regarding theta in the ACC as a correlate of cognitive controls (references in manuscript). We did interrogate other bands as a sanity check and the results were mostly limited to theta. Given the scope of our manuscript and the concerns raised regarding complexity we are concerned that adding frequency analyses beyond theta obfuscates the take home message.

However, the spectrograms in Figure 3 show a range of frequencies and highlight the ones in the theta band as the most dynamic prior to the choice. 

(b) Power spectra and time-frequency analyses may justify the authors focus. I would show these (yaxis - frequency, x-axis - time, z-axis, power).

Thank you for the suggestion. We have added this to Figure 3.    

(7) PC3 as an autocorrelation doesn't seem the to be right way to infer theta entrainment or spikefield relationships, as PCA can be vulnerable to phantom oscillations, and coherence can be transient. It is also difficult to compare to traditional measures of phase-locking. Why not simply use spike-field coherence? This is particularly important with reference to the human literature, which the authors invoke.

Excellent suggestion. Note that PCA provided a way to classify neurons that exhibited peaks in the autocorrelation at theta frequencies. We have added spike-field coherence, and this analysis confirms the differences in theta entrainment of the spike trains across the behavioral groups. Please see Figure 6D.   

Reviewer #3 (Public Review):

Summary:

The study investigated decision making in rats choosing between small immediate rewards and larger delayed rewards, in a task design where the size of the immediate rewards decreased when this option was chosen and increased when it was not chosen. The authors conceptualise this task as involving two different types of cognitive effort; 'resistance-based' effort putatively needed to resist the smaller immediate reward, and 'resource-based' effort needed to track the changing value of the immediate reward option. They argue based on analyses of the behaviour, and computational modelling, that rats use different strategies in different sessions, with one strategy in which they consistently choose the delayed reward option irrespective of the current immediate reward size, and another strategy in which they preferentially choose the immediate reward option when the immediate reward size is large, and the delayed reward option when the immediate reward size is small. The authors recorded neural activity in anterior cingulate cortex (ACC) and argue that ACC neurons track the value of the immediate reward option irrespective of the strategy the rats are using. They further argue that the strategy the rats are using modulates their estimated value of the immediate reward option, and that oscillatory activity in the 6-12Hz theta band occurs when subjects use the 'resistancebased' strategy of choosing the delayed option irrespective of the current value of the immediate reward option. If solid, these findings will be of interest to researchers working on cognitive control and ACCs involvement in decision making. However, there are some issues with the experiment design, reporting, modelling and analysis which currently preclude high confidence in the validity of the conclusions.

Strengths:

The behavioural task used is interesting and the recording methods should enable the collection of good quality single unit and LFP electrophysiology data. The authors recorded from a sizable sample of subjects for this type of study. The approach of splitting the data into sessions where subjects used different strategies and then examining the neural correlates of each is in principle interesting, though I have some reservations about the strength of evidence for the existence of multiple strategies.

Thank you for the positive comments. 

Weaknesses:

The dataset is very unbalanced in terms of both the number of sessions contributed by each subject, and their distribution across the different putative behavioural strategies (see table 1), with some subjects contributing 9 or 10 sessions and others only one session, and it is not clear from the text why this is the case. Further, only 3 subjects contribute any sessions to one of the behavioural strategies, while 7 contribute data to the other such that apparent differences in brain activity between the two strategies could in fact reflect differences between subjects, which could arise due to e.g. differences in electrode placement. To firm up the conclusion that neural activity is different in sessions where different strategies are thought to be employed, it would be important to account for potential cross-subject variation in the data. The current statistical methods don't do this as they all assume fixed effects (e.g. using trials or neurons as the experimental unit and ignoring which subject the neuron/trial came from).

In the revised manuscript we have updated the group assignments. We have improved our description of the logic and methods for employing these groupings as well. With this new approach, all sessions are now included in the analysis. The group assignments are made purely on the behavioral statistics of an animal in each session. We feel this approach is preferable to eliminating neurons or session with the goal of balancing them, which may introduce bias. Further, the rats that contribute the most sessions also tend to be represented across the behavioral groups therefore it is unlikely that effort allocation strategies across groupings are an esoteric feature of an animal. As neurons are randomly sampled from each animal on a given session, we feel that we’re justified in treating these as fixed effects.   

It is not obvious that the differences in behaviour between the sessions characterised as using the 'G1' and 'G2' strategies actually imply the use of different strategies, because the behavioural task was different in these sessions, with a shorter wait (4 seconds vs 8 seconds) for the delayed reward in the G1 strategy sessions where the subjects consistently preferred the delayed reward irrespective of the current immediate reward size. Therefore the differences in behaviour could be driven by difference in the task (i.e. external world) rather than a difference in strategy (internal to the subject). It seems plausible that the higher value of the delayed reward option when the delay is shorter could account for the high probability of choosing this option irrespective of the current value of the immediate reward option, without appealing to the subjects using a different strategy.

Further, even if the differences in behaviour do reflect different behavioural strategies, it is not obvious that these correspond to allocation of different types of cognitive effort. For example, subjects' failure to modify their choice probabilities to track the changing value of the immediate reward option might be due simply to valuing the delayed reward option higher, rather than not allocating cognitive effort to tracking immediate option value (indeed this is suggested by the neural data). Conversely, if the rats assign higher value to the delayed reward option in the G1 sessions, it is not obvious that choosing it requires overcoming 'resistance' through cognitive effort.

The RL modelling used to characterise the subject's behavioural strategies made some unusual and arguably implausible assumptions:

Thank you for the feedback, based on these comments (and those above) we have completely reworked the RL model. In addition, we’ve taken care to separate out the variables that correspond to a resistance- versus a resource-based signal. 

There were also some issues with the analyses of neural data which preclude strong confidence in their conclusions:

Figure 4I makes the striking claim that ACC neurons track the value of the immediately rewarding option equally accurately in sessions where two putative behavioural strategies were used, despite the behaviour being insensitive to this variable in the G1 strategy sessions. The analysis quantifies the strength of correlation between a component of the activity extracted using a decoding analysis and the value of the immediate reward option. However, as far as I could see this analysis was not done in a cross-validated manner (i.e. evaluating the correlation strength on test data that was not used for either training the MCML model or selecting which component to use for the correlation). As such, the chance level correlation will certainly be greater than 0, and it is not clear whether the observed correlations are greater than expected by chance.

We have added more rigorous methods to assess the ival tracking signal (Figure 4 and 5). In addition, we’ve dropped the claim that ival tracking is the same across the behavioral groups. We suspect that this was an artifact of a suboptimal group assignment approach in the previous version. 

An additional caveat with the claim that ACC is tracking the value of the immediate reward option is that this value likely correlates with other behavioural variables, notably the current choice and recent choice history, that may be encoded in ACC. Encoding analyses (e.g. using linear regression to predict neural activity from behavioural variables) could allow quantification of the variance in ACC activity uniquely explained by option values after controlling for possible influence of other variables such as choice history (e.g. using a coefficient of partial determination).

We agree that the ival tracking signal may be influenced by other variables – especially ones that are not cognitive but rather more generated by the autonomic system. We have included a discussion of this possibility in the Discussion section. Our previous work has explored the role of choice history on neural activity, please see White et al., (2024). 

Figure 5 argues that there are systematic differences in how ACC neurons represent the value of the immediate option (ival) in the G1 and G2 strategy sessions. This is interesting if true, but it appears possible that the effect is an artefact of the different distribution of option values between the two session types. Specifically, due to the way that ival is updated based on the subjects' choices, in G1 sessions where the subjects are mostly choosing the delayed option, ival will on average be higher than in G2 sessions where they are choosing the immediate option more often. The relative number of high, medium and low ival trials in the G1 and G2 sessions will therefore be different, which could drive systematic differences in the regression fit in the absence of real differences in the activity-value relationship. I have created an ipython notebook illustrating this, available at: https://notebooksharing.space/view/a3c4504aebe7ad3f075aafaabaf93102f2a28f8c189ab9176d48 07cf1565f4e3. To verify that this is not driving the effect it would be important to balance the number of trials at each ival level across sessions (e.g. by subsampling trials) before running the regression.

This is an excellent point and lead us to abandon the linear regression-based approach to quantify differences in ival coding across behavioral groups.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This paper was extremely hard to read. In addition to the issues raised in the public review (overly complex and incomplete analyses), one of the hardest things to deal with was the writing.

Thank you for the feedback. Hopefully we have addressed this with our thorough rewrite. 

The presentation was extremely hard to follow. I had to read through it several times to figure out what the task was. It wasn't until I got to the RL model Figure 2A that I realized what was really going on with the task. I strongly recommend having an initial figure that lays out the actual task (without any RL or modeling assumptions) and identifies the multiple different kinds of sessions. What is the actual data you have to start with? That was very unclear.

Excellent idea. We have implemented this in Figure 1.  

Labeling session by "group" is very confusing. I think most readers take "group" as the group of subjects, but that's not what you mean at all. You mean some sessions were one way and some were another. (And, as I noted in the public review, you ignore many of the sessions, which I think is not OK.) I think a major rewrite would help a lot. Also, I don't think the group analysis is necessary at all. In the public review, I recommend doing the analyses very differently and more classically.

We have updated the group assignments in a manner that is more intuitive, reflects the delays, and includes all sessions.  

The paper is full of arbitrary abbreviations that are completely unnecessary. Every time I came to "ival", I had to translate that into "number of pellets delivered on the immediate lever" and every time I came to dLP, I had to translate that into "delayed lever press". Making the text shorter does not make the text easier to read. In general, I was taught that unless the abbreviation is the common term (such as "DNA" not "deoxyribonucleic acid"), you should never use an abbreviation. While there are some edge cases (ACC probably over "anterior cingulate cortex"), dLP, iLP, dLPs, iLPs, ival, are definitely way over the "don't do that" line.

We completely agree here and apologize for the excessive use of abbreviations. We have removed nearly all of them

The figures were incomplete, poorly labeled, and hard to read. A lot of figures were missing, for example

Basic task structure

Basic behavior on the task

Scatter plot of the measures that you are clustering (lever press choice X number of pellets on the immediate lever, you can use color or multiple panels to indicate the delay to the delayed lever) Figure 3 is just a couple of examples. That isn't convincing at all.

Figure 4 is missing labels. In Figure 4, I don't understand what you are trying to say.

I don't see how the results on page 16 arise from Figure 6. I strongly recommend starting from the actual data and working your way to what it means rather than forcing this into this unreasonable "session group" analysis.

We have completely reworked the Figures for clarity and content. 

The statement that "no prior study has explored the cellular correlates of cognitive effort" is ludicrous and insulting. There are dozens of experiments looking at ACC in cognitive effort tasks, in humans, other primates, and rodents. There are many dozens of experiments looking at cellular correlates in intertemporal choice tasks, some with neural manipulations, some with ensemble recordings. There are many dozens of experiments looking at cellular relationships to waiting out a delay.

We agree that our statement was extremely imprecise. We have updated this to say:  “Further, a role for theta oscillations in allocating physical effort has been identified. However, the cellular

mechanisms within the ACC that control and deploy types of cognitive effort have not been identified.”

Reviewer #2 (Recommendations For The Authors):

In Figure 2, the panels below E and F are referred to as 'right' - but they are below? I would give them letters.

I would make sure that animal #s, neuron #s, and LFP#s are clearly presented in the results and in each figure legend. This is important to follow the results throughout the manuscript.

Some additional proofreading ('Fronotmedial') might help with clarity.

Based on our updates, this is no longer relevant.  

Reviewer #3 (Recommendations For The Authors):

In addition to the suggestions above to address specific issues, it would be useful to report some additional information about aspects of the experiments and analyses:

Specify how spike sorting was performed and what metrics were used to select well isolated single units.

Done.

Provide histology showing the recording locations for each subject.

Histological assessments of electrodes placements are provided in White et al. 2024, but we provide an example placement. This has been added to the text. 

Indicate the sequence of recording sessions that occurred for each subject, including for each session what delay duration was used and which dataset the session contributed to, and indicate when the neural probes were advanced between sessions.

We feel that this adds complexity unnecessarily as we make no claims about holding units across sessions for differences in coding in the dorsoventral gradient of ACC. 

Indicate the experimental unit when reporting uncertainty measures in figure legends (e.g. mean +/- SEM across sessions).

Done.

Author response:

Before providing a brief provisional response to the two reviews, it is important to reiterate a few key points about our work. First, our paper is largely a computational biophysics paper, augmented by experimental results. Generally speaking, computational biophysics work intends to achieve one of two things (or both). One is to provide more molecular level insight into various behaviors of biomolecular systems that have not been (or cannot be) provided by qualitative experimental results alone. The second general goal of computational biophysics it to formulate new hypotheses to be tested subsequently by experiment. In our paper, we have achieved both of these goals and then confirmed the key computational results by experiment..

The first reviewer has some valuable points, which can be addressed as follows (and will be emphasized in the revised version of the paper): (1) Yes the simulations of capsid rupture in the NPC and capsid-only are directly comparable as both have approximately the same number of bound LEN, as determined by following the LEN-capsid interaction protocol described in the main text (around Fig 6) and in the SI section S3; (2) While we have stressed this point in several places in the manuscript, here again we stress that coarse-grained (CG) MD time is not the same as real time. The point of CG simulations is to accelerate the timescale of the MD and the associated sampling, so the CG “time” from the MD integrator needs to be rescaled to associate a real time to it. As such, our CG simulation is not representing a microsecond of real time but rather something much longer. We will emphasize this again in the revised text. (3) Actually, we think that the parameterization of the LEN model and the LEN-capsid interactions is well described in the text associated with Fig 6 and in SI section S3. It is true that this one part of the CG model was parameterized “top-down” given the good experimental structures of bound LEN to capsid and other data, but the rest of the CG model is “bottom-up” (meaning developed from well-defined coarse-graining statistical mechanics as applied to molecular level structures and interactions, see also below). 

As for the second reviewer, this review is quite problematic in our view as the reviewer seems to think that quoting a number of qualitative experimental results is sufficient to undermine the impact of our paper (they are not) and, furthermore, the reviewer appears to have a very minimal understanding of “bottom-up” CG modeling, which we have utilized. This modeling does not in fact rely on the “assumptions” this reviewer alleges we have relied on. (As an aside, it could be helpful for this reviewer to study the review by Jin et al, https://doi.org/10.1021/acs.jctc.2c00643) in order to become more familiar with the field and our approach before criticizing it.) We also note that our main HIV capsid-NPC docking model is already published in PNAS (https://doi.org/10.1073/pnas.2313737121), where it underwent rigorous peer review. In our forthcoming full response to the reviews and in the revised paper we will attempt to address a number of this reviewers comments, but the number, extent, and tone of this collection of criticisms, for us, calls into question the objectivity of this reviewer, not to mention the reviewer’s rather weak understanding of what we have done and how we have done it.

Finally, while we certainly appreciate the overall positive eLife assessment, we are disappointed by the statement “some mechanistic interpretations rely on assumptions embedded in the simulations, leaving parts of the evidence incomplete”. Of course, all simulations (and experiments) rely on certain assumptions, but we have gone to great length to provide a “bottomup” approach to our modeling, based on underlying molecular level structures and interactions, and we have provided experimental validation of the main simulation predictions. It seems that the comments of the second reviewer may have influenced this point of view, but we do not feel it is justified.

Reviewer #2 (Public review):

Summary:

Previous studies by some of the same authors of the actual manuscript showed that healthy human newborns memorize recently learned nonsense words. They exposed neonates to a familiarization period (several minutes) when multiple repetitions of a bisyllabic word were presented, uttered by the same speaker. Then they exposed neonates to an "interference period" when newborns listened to music or the same speaker uttering a different pseudoword. Finally, neonates were exposed to a test period when infants hear the familiarized word again. Interestingly, when the interference was music, the recognition of the word remained. The word recognition of the word was measured by using the NIRS technique, which estimates the regional brain oxygenation at the scalp level. Specifically, the brain response to the word in the test was reduced, unveiling a familiarity effect, while an increase in regional brain oxygenation corresponds to the detection of a "new word" due to a novelty effect. In previous studies, music does not erase the memory traces for a word (familiarity effect), while a different word uttered by the same speaker does.

The current study aims at exploring whether and how word memory is interfered with by other speech properties, specifically the changes in the speaker, while young children can distinguish speakers by processing the speech. The author's main hypothesis anticipates that new speaker recognition would produce less interference in the familiarized word because somehow neonates "separate" the processing of both words (familiarized uttered by one speaker, and interfering word, uttered by a different speaker), memorizing both words as different auditory events.

From my point of view, this hypothesis is interesting, since the results would contribute to estimating the role of the speaker in word learning and speech processing early in life.

Strengths:

(1) New data from neonates. Exploring neonates' cognitive abilities is a big challenge, and we need more data to enrich the knowledge of the early steps of language acquisition.

(2) The study contributes new data showing the role of speaker (recognition) on word learning (word memory), a quite unexplored factor. The idea that neonates include speakers in speech processing is not new, but its role in word memory has not been evaluated before. The possible interpretation is that neonates integrate the process of the linguistic and communicative aspects of speech at this early age.

(3) The study proposes a quite novel analytic approach. The new mixed models allow exploring the brain response considering an unbalanced design. More than the loss of data, which is frequent in infants' studies, the familiarization, interference and learning processes may take place at different moments of the experiment (e.g. related to changes in behavioural states along the experiment) or expressed in different regions (e.g. related to individual variations in optodes' locations and brain anatomy).

Weaknesses:

I did not find major weaknesses. However, I would like to have more discussion or explanation on the following points.

(1) It would be fine to report the contribution of each infant to the analysis, i.e. how many good blocks, 1 to 5 in sequence 1 and 2, were provided by each infant.

(2) Why did the factor "blocknumber" range from 0 to 4? The authors should explain what block zero means and why not 1 to 5.

(3) I may suggest intending to integrate the changes in brain activity across the 3 phases. That is, whether changes in familiarization relate to changes in the test and interference phases. For instance, in Figure 2, the brain response distinguishes between same and novel words that occurred over IFG and STG in both hemispheres. However, in the right STG there was no initial increase in the brain response, and the response for the same was higher than the one for novels in the 5th block.

(4) Similarly, it is quite amazing that the brain did not increase the activity with respect to the familiarization during the interference phase, mainly over the left hemisphere, even if both the word and speaker changed. Although the discussion considers these findings, an integrated discussion of the detection of novel words and the detection of a novel speaker over time may benefit from a greater integration of the results.

Appraisal:

The authors achieved their aims because the design and analytic approaches showed significant differences. The conclusions are based on these results. Specifically, the hypothesis that neonates would memorize words after interference, when interfered speech is pronounced by a different speaker, was supported by the data in blocks 2 and 5, and the potential mechanisms underlying these findings were discussed, such as separate processing for different speakers, likely related to the recognition of speaker identity.

I think the discussion is well-structured, although I may suggest integrating the changes into the three phases of the study. Maybe comparing with other regions, not related to speech processing.

Evaluating neonates is a challenge. Because physiology is constantly changing. For instance, in 9 minutes, newborns may transit from different behavioral states and experience different physiological needs.

This study offers the opportunity to inspire looking for commonalities and individual differences when investigating early memory capacities of newborns.

This made me think about how in my own household, which I manage mostly on my own, the things I rely on, such as housing and education systems and how they exist because of the colonial systems, even though they may appear to me as just "regular" life.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

In this paper, the authors develop a biologically plausible recurrent neural network model to explain how the hippocampus generates and uses barcode-like activity to support episodic memory. They address key questions raised by recent experimental findings: how barcodes are generated, how they interact with memory content (such as place and seed-related activity), and how the hippocampus balances memory specificity with flexible recall. The authors demonstrate that chaotic dynamics in a recurrent neural network can produce barcodes that reduce memory interference, complement place tuning, and enable context-dependent memory retrieval, while aligning their model with observed hippocampal activity during caching and retrieval in chickadees.

Strengths:

(1) The manuscript is well-written and structured.

(2) The paper provides a detailed and biologically plausible mechanism for generating and utilizing barcode activity through chaotic dynamics in a recurrent neural network. This mechanism effectively explains how barcodes reduce memory interference, complement place tuning, and enable flexible, context-dependent recall.

(3) The authors successfully reproduce key experimental findings on hippocampal barcode activity from chickadee studies, including the distinct correlations observed during caching, retrieval, and visits.

(4) Overall, the study addresses a somewhat puzzling question about how memory indices and content signals coexist and interact in the same hippocampal population. By proposing a unified model, it provides significant conceptual clarity.

Weaknesses:

The recurrent neural network model incorporates assumptions and mechanisms, such as the modulation of recurrent input strength, whose biological underpinnings remain unclear. The authors acknowledge some of these limitations thoughtfully, offering plausible mechanisms and discussing their implications in depth.

One thread of questions that authors may want to further explore is related to the chaotic nature of activity that generates barcodes when recurrence is strong. Chaos inherently implies sensitivity to initial conditions and noise, which raises questions about its reliability as a mechanism for producing robust and repeatable barcode signals. How sensitive are the results to noise in both the dynamics and the input signals? Does this sensitivity affect the stability of the generated barcodes and place fields, potentially disrupting their functional roles? Moreover, does the implemented plasticity mitigate some of this chaos, or might it amplify it under certain conditions? Clarifying these aspects could strengthen the argument for the robustness of the proposed mechanism.

In our model, chaos is used to produce a random barcode when forming memories, but memory retrieval depends on attractor dynamics. Specifically, the plasticity update at the end of the cache creates an attractor state, and then afterwards for successful memory retrieval the network activity must settle into this attractor rather than remaining chaotic. This attractor state is a conjunction of memory content (place and seed activity) and memory index (barcode activity). Thus a barcode is ‘reactivated’ when network dynamics during retrieval settle into this cache attractor, or in other words chaotic dynamics do not need to generate the same barcode twice.

The reviewer raises an important point, which is how sensitivity to initial conditions and noise would affect the reliability of our proposed mechanism. The key question here is how noise will affect the network’s dynamics during retrieval. Would adding noise to the dynamics make memory retrieval more difficult? We thank the reviewer for suggesting we investigate this further, and below describe our experiments and changes to the manuscript to better address this topic.

We first experimented with adding independent gaussian distributed noise into each unit, drawn independently at each timestep. We analyzed recall accuracy using the same task and methods as Fig. 4F while varying the magnitude of noise. Memory recall was quite robust to this form of noise, even as the magnitude of noise approached half of the signal amplitude. This first experiment added noise into the temporal dynamics of the network. We subsequently examined adding static noise into the network inputs, which can also be thought of as introducing noise into initial conditions. Specifically, we added independent gaussian distributed noise into each unit, with the random value held constant for the extent of temporal dynamics. This perturbation decreased the likelihood of memory recall in a graded manner with noise magnitude, without dramatically changing the spatial profile. Examination of dynamics on individual trials revealed that the network failed to converge onto a cache attractor on some random fraction of trials, with other trials appearing nearly identical to noiseless results. We now include these results in the text and as a new supplementary figure, Figure S4AB.

To clarify the network dynamics and the purpose of chaos in our model, we make the following modifications in text:

Section 2.3, paragraph 2 (starting at “To store memories…”):

“…place inputs arrive into the RNN, recurrent dynamics generate an essentially random barcode, seed inputs are activated, and then Hebbian learning binds a particular pattern of barcode activity to place- and seed-related activity.”

Section 2.3, paragraph 3 (starting at “Memory recall in our network…”): As an example, consider a scenario in which an animal has already formed a memory at some location l, resulting in the storage of an attractor \vec{a} into the RNN. The attractor \vec{a} can be thought of as a linear combination of place input-driven activity $p(l)$, seed input-driven activity $s$, and a recurrent-driven barcode component $b$. Later, the animal returns to the same location and attempts recall (i.e. sets r \= 1, Figure 3B). Place inputs for location l drive RNN activity towards $p(l)$, which is partially correlated with attractor \vec{a}, and the recurrent dynamics cause network activity to converge onto attractor \vec{a}. In this way, barcode activity $b$ is reactivated, along with the place and seed components stored in the attractor state, $p(l)$ and $s$. The seed input can also affect recall, as discussed in the following section.

Section 2.4, final paragraph (starting “We further examined how model hyperparameters affected performance on these tasks”), added the following describing new results on adding noise: We found that adding noise to the network's temporal dynamics had little effect on memory recall performance (Figure S4A). However, large static noise vectors added to the network's input and initial state decreased the overall probability of memory recall, but not its spatial profile (Figure S4B).

It may also be worth exploring the robustness of the results to certain modeling assumptions.  For instance, the choice to run the network for a fixed amount of time and then use the activity  at the end for plasticity could be relaxed.

As described above, chaotic dynamics are necessary to generate a barcode during a cache, but not to reactivate that barcode during retrieval. During a successful memory retrieval, network activity settles into an attractor state and thus does not depend on the duration of simulated dynamics. The choice of duration to run dynamics during caching is important, but only insofar as activity significantly decorrelates from the initial state. We show in Figure S1B that decorrelation saturates ~t=25, and thus any random time point t > 25 would be similarly effective. We used a fixed duration runtime for caches only to avoid introducing unnecessary complication into our model.

Reviewer #2 (Public review):

Summary:

Striking experimental results by Chettih et al 2024 have identified high-dimensional, sparse patterns of activity in the chickadee hippocampus when birds store or retrieve food at a given site. These barcode-like patterns were interpreted as "indexes" allowing the birds to retrieve from memory the locations of stored food.

The present manuscript proposes a recurrent network model that generates such barcode activity and uses it to form attractor-like memories that bind information about location and food. The manuscript then examines the computational role of barcode activity in the model by simulating two behavioral tasks, and by comparing the model with an alternate model in which barcode activity is ablated.

Strengths of the study:

Proposes a potential neural implementation for the indexing theory of episodic memory - Provides a mechanistic model of striking experimental findings: barcode-like, sparse patterns of activity when birds store a grain at a specific location

A particularly interesting aspect of the model is that it proposes a mechanism for binding discrete events to a continuous spatial map, and demonstrates the computational advantages of this mechanism.

Weaknesses:

The relation between the model and experimentally recorded activity needs some clarification

The relation with indexing theory could be made more clear

The importance of different modeling ingredients and dynamical mechanisms could be made more clear

The paper would be strengthened by focusing on the most essential aspects

Comments:

The model distinguishes between "barcode activity" and "attractors". Which of the two corresponds to experimentally-recorded barcodes? I would presume the attractors. A potential issue is that the attractors are, as explained in the text (l.137), conjunctions of place activity, barcode activity and "seed" inputs. The fact that the seed activity is shared across attractors seems to imply that they have a non-zero correlation independent of distance. Is that the case in the model? If I understand correctly, Fig 3D shows correlations between an attractor and barcodes at different locations, but correlations between attractors at different locations are not shown. Fig 1 F instead shows that correlations between recorded retrieval activities decay to zero with distance.

More generally, the fact that the expression "barcode" is apparently used with different meanings in the model and in the experiments is potentially confusing (in the model they correspond to activity generating during caching, and this activity is distinct from the memories; my understanding is that in the experiments barcodes correspond to both caching and retrieval, but perhaps I am mistaken?).

Our intent is to use the expression “barcode” as similarly as possible between model and experimental work. The reviewer points out that the connection between barcodes in experimental and modeling work is unclear, as well as the relation of “attractors” in our model to previous experimental results. The meaning of ‘barcode’ is absolutely critical—we clarify below our intended meaning, and then describe changes to the manuscript to highlight this.

In experiments, we observed that activity during caching looked different than ordinary hippocampal activity (i.e. typical “place activity” observed during visits). Empirically there were two major differences. First, there was a pattern of neural activity which was present during every cache . This pattern was also present when birds visually inspected sites containing a cached seed, but not when visually inspecting an empty site. This is what we refer to as “seed activity”. Second, there was a pattern of neural activity which was unique to each cache. This pattern re-occurred during retrieval, and was orthogonal to place activity (see Fig. 1E-F). This is what we refer to as “barcode activity”. In summary, activity during a cache (or retrieval) contains a combination of three components: place activity, seed activity, and barcode activity.

These experimental findings are recapitulated in our model, as activity during a cache contains a combination of three components: place activity driven by place inputs, seed activity driven by seed inputs, and barcode activity generated by recurrent dynamics. Cache activity in the model corresponds to cache activity in experiments, and barcodes in the model correspond to barcodes in experiments. Our model additionally has “attractors”, meaning that network connectivity changes so that the activity generated during a simulated cache becomes an attractor state of network dynamics. “Attractors” refers to a feature of network dynamics, not a distinct activity state, and we do not yet know if these attractors exist in experimental data.

Figure 3D, as described in the figure legend, is a correlation of activity during cache and retrieval (in purple), for cache-retrieval pairs at the same or at different sites. We believe this is what the reviewer asks to see: the correlation between attractor states for different cache locations. The reviewer makes an important point: seed activity is shared across all attractors, so then why are correlations not high for all locations? This is because attractors also have a place component, which is anti-correlated for distant locations. This is evident in Fig. 3D by noticing that visit-visit correlations (black line, corresponding to place activity only) are negative for distant locations, and the correlation between attractors (purple line, cache-retrieval pairs) is subtly shifted up relative to the black line (place code only) for these distant locations. The size of this shift is due to the relative magnitude of place and seed inputs. For example, if we increase the strength of the seed input during caching (blue line), we can further increase the correlation between attractors even for quite distant sites:

Author response image 1.

To clarify the manuscript, we made the following modifications:

Section 2.2, first paragraph: We model the hippocampus as a recurrent neural network (RNN) (Alvarez and Squire, 1994; Tsodyks, 1999; Hopfield, 1982) and propose that recurrent dynamics can generate barcodes from place inputs. As in experiments, the model’s population activity during a cache should exhibit both place and barcode activity components.

Section 2.3, paragraph 3 (starting at “Memory recall in our network…”): As an example, consider a scenario in which an animal has already formed a memory at some location l , resulting in the storage of an attractor \vec{a} into the RNN . The attractor \vec{a} can be thought of as a linear combination of place input-driven activity $p(l)$, seed input-driven activity $s$, and a recurrent-driven barcode component $b$. Later, the animal returns to the same location and attempts recall (i.e. sets r \= 1, Figure 3B). Place inputs for l drive RNN activity towards $p(l)$, which is partially correlated with attractor \vec{a}, and the recurrent dynamics cause network activity to converge onto attractor \vec{a}. In this way, barcode activity $b$ is reactivated as part of attractor \vec{a}, along with the place and seed components stored in the attractor state, $p(l)$ and $s$. The seed input can also affect recall, as discussed in the following section.

The insights obtained from the network model for the computational role of barcode activity could be explained more clearly. The introduction starts by laying out the indexing theory, which proposes that the hippocampus links an index with each memory so that the memory is reactivated when the index is presented. The experimental paper suggests that the barcode activations play the role of indexes. Yet, in the model reactivations of memories are driven not by presenting bar-code activity, but by presenting place activity (Cache Presence task) or seed activity (Cache Location task). So it seems that either place activity and seed activity play the role of indexes. Section 2.5 nicely shows that ultimately the role of barcode activity is to decorrelate attractors, which seems different from playing the role of indexes. I feel it would be useful that the Discussion reassess more critically the relationship between barcodes, indexing theory, and key-value architectures.

The reviewer highlights a failure on our part to clearly identify the connection between our findings on barcodes, indexing theory, and key-value architectures. This is another major component of the paper, and below we propose changes to the manuscript to clarify these concepts and their relationships. First, we will summarize the key points that were unclear in our original manuscript.

The reviewer equates the concept of an ‘index’ with that of a ‘query’: the signal that drives memory reactivation. This may be intuitive, but it is not how a memory index was defined in indexing theory (e.g. Teyler & DiScenna 1986). In indexing theory, the index is a pattern of hippocampal activity that is (a) generated during memory formation, (b) separate from the activity encoding memory content, and (c) linked to memory content via associative plasticity. After memory formation, a memory might be queried by activating a partial set of the memory contents, which would then drive reactivation of the hippocampal index, leading to pattern completion of memory contents. See, for example, figure 1 of Teyler and DiScenna 1986. The ‘index’ is thus not the same as the ‘query’ that drives recall.

We propose in this work that barcode activity is such an index. Indexing theory originally posited that memory content was encoded by neocortex, and memory index was encoded by hippocampus. However the experiments of Chettih et al. 2024 revealed that the hippocampus contained both memory content and memory index signals, and furthermore there was no division of cells into ‘content’ and ‘index’ subtypes. Thus our model drops the assumption of earlier work that index and content signals correspond to different neurons in different brain areas—a significant advance of our work. Otherwise, the experimentally observed barcodes and the barcodes generated by our computational model play the role of indices as originally defined.

Our original manuscript was unclear on the relationship of indexing theory and key-value systems. Our work connects diverse areas of memory models, including attractor dynamics, key-value memory systems, and memory indexing. A full account of these literatures and their relationships may be beyond the scope of this manuscript, and we note that a recent review article (Gershman, Fiete, and Irie, 2025) further clarifies the relationship between key-value memory, indexing theory, and the hippocampus. We will cite this work in our discussion as a source for the interested reader.

Briefly, a key-value memory system distinguishes between the address where a memory is stored, the ‘key’, and the content of that memory, the ‘value’. An advantage of such systems is that keys can be optimized for purposes independent of the value of each memory. The use of barcodes in our model to decorrelate memories is related to this optimization of keys in key-value memory systems. By generating barcodes and adding this to the attractor state corresponding to a cache memory, the ‘address’ of the memory in population activity is differentiated from other memories. Our work is thus consistent with the idea that hippocampus generates keys and implements a key storage system. However it is not so straightforward to equate barcodes with keys, as they are defined in key-value memory. As the reviewer points out, memory recall can be driven by location and seed inputs, i.e. it is content-addressable. We think of the barcode as modifying the memory address to better separate similar memories, without changing memory content, and the resulting memory can be recalled by querying with either content or barcode. Given the complex and speculative nature of these relationships, we prefer to note the salient connection of our work with ongoing efforts applying the key-value framework to biological memory, and leave the precise details of this connection to future work.

We make the following changes in the manuscript to clarify these ideas:

Introduction, first paragraph: In this scheme, during memory formation the hippocampus generates an index of population activity, and the neurons representing this index are linked with the neurons representing memory content by associative plasticity . Later, re-experience of partial memory contents may reactivate the index, and reactivation of the index drives complete recall of the memory contents.

Discussion, 4th paragraph on key-value: Interestingly, prior theoretical work has suggested neural implementations for both key-value memory and attention mechanisms, arguing for their usefulness in neural systems such as long term memory (Kanerva, 1988; Tyulmankov et al., 2021; Bricken and Pehlevan, 2021; Whittington et al., 2021; Kozachkov et al., 2023; Krotov and Hopfield, 2020; Gershman 2025 ). In this framework, the address where a memory is stored (the key) may be optimized independently of the value or content of the memory. In our model, barcodes improve memory performance by providing a content-independent scaffold that binds to memory content, preventing memories with overlapping content from blurring together. Thus barcodes can be considered as a change in memory address, and our model suggests important connections between recurrent neural activity and key generation mechanisms. However we note that barcodes should not be literally equated with keys in key-value systems as our model’s memory is ‘content-addresable’—it can be queried by place and seed inputs.

The model includes a number of non-standard ingredients. It would be useful to explain which of these ingredients and which of the described mechanisms are essential for the studied phenomenon. In particular:

- the dynamics in Eq.2 include a shunting inhibition term. Is it essential and why?

The shunting inhibition is important as it acts to normalize the network activity to prevent runaway excitation. We hope to clarify this further by amending the following sentence in section 2.2: “g (·) is a leak rate that depends on the average activity of the full network, representing a form of global shunting inhibition that normalizes network activity to prevent runaway excitation from recurrent dynamics.”

- same question for the global inhibition included in the random connectivity;

The distribution from which connectivity strengths are drawn has a negative mean (global inhibition). This causes activity during caching (i.e. r = 1) to be sparser than activity during visits (i.e. r = 0), and was chosen to match experimental findings. In figures 2B and S2B we show that our model can transition between a mode with place code only, barcode only, or a mode containing both, by changing the variance of the weight distribution while holding the mean constant. We suggest clarifying this by editing the following in section 2.2, paragraph 2: “We initialize the recurrent weights from a random Gaussian distribution, . where 𝑁_𝑋 is the number of RNN neurons and μ < 0, reflecting global subtractive inhibition that encourages sparse network activity to match experimental findings (Chettih et al. 2024).”

- the model is fully rate-based, but for certain figures, spikes are randomly generated. This seems superfluous.

Spikes are simulated for one analysis and one visualization, where it is important to consider noise or variability in neural responses across trials. First, for Fig. 2H,J, we generated spikes to allow a visual comparison to figures that can be easily generated from experimental data. Second, and more significantly, for the analysis underlying Fig. 3D, it is essential to simulate variability in neural responses. Because our rate-based models are noiseless, the RNN’s rate vector at site distance = 0 will always be the same and result in a correlation of 1 for both visit-visit and cache-retrieval. However, we show that, if one interprets the rate as a noisy Poisson spiking process, the correlation at site distance = 0 between a cache-retrieval pair is higher than that of two visits. This is because under a Poisson spiking model, the signal-to-noise ratio is higher for cache-retrieval activity, where rates are higher in magnitude. The greater correlation for a cache-retrieval pair at the same site, relative to visits at the same site, is an experimental finding that was critical for our model to reproduce. We detail clarifications to the manuscript below in response to the reviewer’s following and related question.

How are the correlations determined in the model (e.g., Fig 2 B)? The methods explain that they are computed from Poisson-generated spikes, but over which time period? Presumably during steady-state responses, but are these responses time-averaged?

The reviewer points out a lack of clarity in our original manuscript. Correlations for events (caches, retrievals and visits) at different sites are calculated in two sections of the paper (2B, 3D), for different purposes and with slight differences in methods:

- For figure 2B, no spikes are simulated. Note that the methods mentioning poisson spike generation specify only Fig. 2H,J and Fig. 3D. We simply take the network’s rate vector at timestep t=100 (when the decorrelating effect of chaotic dynamics has saturated, S1A-B) and correlate this vector when generated at different locations. We now clarify this in the legend for Figure 2B: “We show correlation of place inputs (gray) and correlation of the RNN's rate vector at t = 100 (black).”

- For Figure 3D, we want to compare the model to empirical results from Chettih et al. 2024, and reproduced in this paper in Fig. 1E-F. These empirical results are derived from correlating vectors of spiking activity on pairs of single trials, and are thus affected by noise or variability in neural responses as described in our response to the reviewer’s previous question. We thus took the RNN’s rate vector at t=100 and simulated spiking data by drawing samples from a poisson distribution to get spike counts. Our original manuscript was unclear about this, and we suggest the following changes:

- Legend for Figure 3D: D. Correlation of Poisson-generated spikes simulated from RNN rate vectors at two sites, plotted as a function of the distance between the two sites.

- Section 2.3, last paragraph: Population activity during retrieval closely matches activity during caching, and is substantially decorrelated from activity during visits (Figure 3C). To compare our model with the empirical results reproduced in Figure 1E,F, we ran in silico experiments with caches and retrievals at varying sites in the circular arena. We simulated Poisson-generated spikes drawn from our network's underlying rates to match the intrinsic variability in empirical data (see Methods).

- Methods, subsection Spatial correlation of RNN activity for cache-retrieval pairs at different sites: To calculate correlation values as in Figure \ref{fig3}D, we simulated experiments where 5 sites were randomly chosen for caching and retrieval. To compare model results to the empirical data in Fig. 1E,F, which includes intrinsic neural variability, we sampled Poisson-generated spike counts from the rates output by our model. Specifically, for RNN activity \vec{r_i} at location i, using the rates at t=100 as elsewhere, we first generate a sample vector of spikes…

I was confused by early and late responses in Fig 2 C. The text says that the activity is initialized at zero, so the response at t=0 should be flat (and zero). More generally, I am not sure I understand why the dynamics matter for the phenomenon at all, presumably the decorrelation shown in Fig 2B depends only on steady state activity (cf previous question).

Thanks for catching this mistake. The legend has been updated to indicate that the ‘early’ response is actually at t=1, when network activity reflects place inputs without the effects of dynamics. The reviewer is correct that we are primarily interested in the ‘late’ response of the network. All other results in the paper use this late response at t=100. As shown in Fig. S2A,B, this timepoint is not truly a steady state, as activity in the network continues to change, but the decorrelation of network activity with place-driven activity has saturated.

We include the early response in Fig. 2C for visual comparison of the purely place-driven early activity with the eventual network response. It is also relevant since, as the reviewer points out above, there is a shunting inhibition term in the dynamics that is present during both low and high recurrent strength simulations.

Related to the previous point, the discussion of decorrelation (l.79 - 97) is somewhat confusing. That paragraph focuses on chaotic activity, but chaos decorrelates responses across different time points. Here the main phenomenon is the decorrelation of responses across different spatial inputs (Fig 2B). This decorrelation is presumably due to the fact that different inputs lead to different non-trivial steady-state responses, but this requires some clarification. If that is correct, the temporal chaos adds fluctuations around these non-trivial steady-state responses, but that alone would not lead to the decorrelation shown in Fig 2B.

We agree with the reviewer that chaotic activity produces a decorrelation across time points. Because of chaotic dynamics, network activity does not settle into a trivial steady-state, and instead evolves from the initial state in an unpredictable way. The network does not settle into a steady-state pattern, but both the decorrelation of network state with initial state and the rate of change in the network state saturate after ~t=25 timesteps, as shown in Fig. S2A-B.

The initial activity for nearby states is similar, due to them receiving similar place inputs.

Because network activity is chaotically decorrelated from this initial state by temporal dynamics, ‘late stage’ network activity between nearby spatial states is less correlated than ‘early stage’ activity. Thus the temporal decorrelation produces a spatial decorrelation. We believe that the changes we have introduced to the manuscript in revision will make this point clearer in our resubmission.

A key ingredient of the model is that the recurrent interactions are switched on and off between "caching" and "visits". The discussion argues that a possible mechanism for this is recurrent inhibition (l.320), which would need to be added. However two forms of inhibition are already included in the model. The text also says that it is unclear how units in the model should be mapped onto E and I neurons. However the model makes explicit assumptions about this, in particular by generating spikes from individual neurons. Altogether, I did not find that part of the Discussion convincing.

We agree with the reviewer that this section is a limitation of our current work, and in fact it is an ongoing area of future research. However we think the advances in this current work warrant publication despite this topic requiring further research. We attempted to discuss this limitation explicitly, and note that the other reviewer pointed this section out as particularly helpful. We do not think it is problematic for a realistic model of the brain to ultimately include 3, or even more forms of inhibition. We do not think that poisson-generated spikes commit us to interpreting network units as single neurons. Spikes are not a core part of our model’s mechanism, and were used only as a mechanism of introducing variability on top of deterministic rates for specific analyses. Furthermore one could still view network units as pools of both E and I spiking neurons. We would welcome further recommendations the reviewer believes are important to note in this section on our model’s limitations.

On lines 117-120 the text briefly mentions an alternate feed-forward model and promptly discards it. The discussion instead says that a "separate possibility is that barcodes are generated in a circuit upstream of where memories are stored, and supplied as inputs to the hippocampal population", and that this possibility would lead to identical conclusions. The two statements seem a bit contradictory. It seems that the alternative possibility would replace the need for switching on and off recurrent interactions, with a mechanism where barcode inputs are switched on and off. This alternate scenario is perhaps more plausible, so it would be useful to discuss it more explicitly.

We apologize for the confusion here, which seems to be due to our phrasing in the discussion section. We do reject the idea that a simple feed-forward model could generate the spatial correlation profile observed in data, as mentioned in the text and included as Fig. S2. Our statement in the discussion may have seemed contradictory because here we intended to discuss the possibility that an upstream area generates barcodes, for example by the chaotic recurrent dynamics proposed in our work, while a downstream network receives these barcodes as inputs and undergoes plasticity to store memories as attractors. We did not intend to suggest any connection to the feedforward model of barcode generation, and apologize for the confusion. Our claim that this ‘2 network’ solution would lead to similar conclusions is because the upstream network would need an efficient means of barcode generation, and the downstream network would need an efficient means of storing memory attractors, and separating these functions into different networks is not likely to affect for example the advantage of partially decorrelating memory attractors. Moreover, the downstream network would still require some form of recurrent gating, so that during visits it exhibits place activity without activating stored memory attractors!

We thus chose a 1 network instead of a 2 network solution because it was simpler and, we believe, more interesting. It is challenging in the absence of more data to say which is more plausible, thus we wanted to mention the possibility of a 2 network solution. We suggest the following changes to the manuscript:

- Discussion, 3rd paragraph: “Alternatively, other mechanisms may be involved in generating barcodes. We demonstrated that conventional feed-forward sparsification (Babadi and Sompolinsky, 2014; Xie et al., 2023) was highly inefficient, but more specialized computations may improve this (Földiak, 1990; Olshausen and Field, 1996; Sacouto and Wichert, 2023; Muscinelli et al., 2023). Another possibility is that barcodes are generated in a separate recurrent network upstream of the recurrent network where memories are stored. In this 2-network scenario, the downstream network receives both spatial tuning and barcodes as inputs. This would not obviate the need for modulating recurrent strength in the downstream network to switch between input-driven modes and attractor dynamics. We suspect separating barcode generation and memory storage in separate networks would not fundamentally affect our conclusions.”

As a minor note, the beginning of the discussion states that the presented model is similar to previous recurrent network models of the hippocampus. It would be worth noting that several of the cited works assign a very different role to recurrent interactions: they generate place cell activity, while the present model assumes it is inherited from upstream inputs.

We are not sure how best to modify the paper to address this suggestion. As far as we know, all of the cited models which deal with spatial encoding do assume that the hippocampus receives a spatially-modulated or spatially-tuned input. For example, the Tsodyks 1999 paper cited in this paragraph uses exponentially-decaying place inputs to each neuron highly similar to our model. Furthermore we explore how our model would perform if we change the format of spatial inputs in Fig. S4, and find key results are unchanged. It is unclear how hippocampal place fields could emerge without inputs that differentiate between spatial locations. We think it is appropriate to highlight the similarity of our model to well known hopfield-type recurrent models, where memories are stored as attractor states of the network dynamics.

On the other hand, we agree that a common line of hippocampal modeling proposes that recurrent interactions reshape spatial inputs to produce place fields. This often arises in the context of hippocampus generating a predictive map, where inputs may be one-hot for a single spatial state, in a grid cell-like format, or a random projection of sensory features. We attempted to address this in section 2.6, using a model which superimposes the random connectivity needed for barcode generation with the structured connectivity needed for predictive map formation. We found that such a model was able to perform both predictive and barcode functions, suggesting a path forward to connecting different lines of hippocampal modeling in future work.

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)):

In this manuscript, Xiong and colleagues investigate the mechanisms operating downstream to TRIM32 and controlling myogenic progression from proliferation to differentiation. Overall, the bulk of the data presented is robust. Although further investigation of specific aspects would make the conclusions more definitive (see below), it is an interesting contribution to the field of scientists studying the molecular basis of muscle diseases.

We thank the Reviewer for appreciating our work and for their valuable suggestions to improve our manuscript. We have carefully addressed some of the concerns raised, as detailed here, while others, which require more experimental efforts, will be addressed as detailed in the Revision Plan.

In my opinion, a few aspects would improve the manuscript. Firstly, the conclusion that Trim32 regulates c-Myc mRNA stability could be expanded and corroborated by further mechanistic studies:

1. Studies investigating whether Tim32 binds directly to c-Myc RNA. Moreover, although possibly beyond the scope of this study, an unbiased screening of RNA species binding to Trim32 would be informative. Authors’ response. This point will be addressed as detailed in the Revision Plan

If possible, studies in which the overexpression of different mutants presenting specific altered functional domains (NHL domain known to bind RNAs and Ring domain reportedly involved in protein ubiquitination) would be used to test if they are capable or incapable of rescuing the reported alteration of Trim32 KO cell lines in c-Myc expression and muscle maturation.

Authors’ response. This point will be addressed as detailed in the Revision Plan

An optional aspect that might be interesting to explore is whether the alterations in c-Myc expression observed in C2C12 might be replicated with primary myoblasts or satellite cells devoid of Trim32.

Authors’ response. This point will be addressed as detailed in the Revision Plan

I also have a few minor points to highlight:

• • It is unclear if the differences highlighted in graphs 5G, EV5D, and EV5E are statistically significant.*

Authors’ response. We thank the Reviewer for raising this point. We now indicated the statistical analyses performed on the data presented in the mentioned figures (according also to a point of Reviewer #3). According to the conclusion that Trim32 is necessary for proper regulation of c-Myc transcript stability, using 2-way-ANOVA, the data now reported as Figure 5G show the statistically significant effect of the genotype at 6h (right-hand graph) but not at D0 (left-hand graph). In the graphs of Fig. EV5 D and E at D0 no significant changes are observed whereas at 6h the data show significant difference at the 40 min time point. We included this info in the graphs and in the corresponding legends.

- On page 10, it is stated that c-Myc down-regulation cannot rescue KO myotube morphology fully nor increase the differentiation index significantly, but the corresponding data is not shown. Could the authors include those quantifications in the manuscript?

Authors’ response. As suggested, we included the graph showing the differentiation index upon c-Myc silencing in the Trim32 KO clones and in the WT clones, as a novel panel in Figure 6 (Fig. 6D). As already reported in the text, a partial recovery of differentiation index is observed but the increase is not statistically significant. In contrast, no changes are observed applying the same silencing in the WT cells. Legend and text were modified accordingly.

Reviewer #1 (Significance (Required)):

The manuscript offers several strengths. It provides novel mechanistic insight by identifying a previously unrecognized role for Trim32 in regulating c-Myc mRNA stability during the onset of myogenic differentiation. The study is supported by a robust methodology that integrates CRISPR/Cas9 gene editing, transcriptomic profiling, flow cytometry, biochemical assays, and rescue experiments using siRNA knockdown. Furthermore, the work has a disease relevance, as it uncovers a mechanistic link between Trim32 deficiency and impaired myogenesis, with implications for the pathogenesis of LGMDR8. * * At the same time, the study has some limitations. The findings rely exclusively on the C2C12 myoblast cell line, which may not fully represent primary satellite cell or in vivo biology. The functional rescue achieved through c-Myc knockdown is only partial, restoring Myogenin expression but not the full differentiation index or morphology, indicating that additional mechanisms are likely involved. Although evidence supports a role for Trim32 in mRNA destabilization, the precise molecular partners-such as RNA-binding activity, microRNA involvement, or ligase function-remain undefined. Some discrepancies with previous studies, including Trim32-mediated protein degradation of c-Myc, are acknowledged but not experimentally resolved. Moreover, functional validation in animal models or patient-derived cells is currently lacking. Despite these limitations, the study represents an advancement for the field. It shifts the conceptual framework from Trim32's canonical role in protein ubiquitination to a novel function in RNA regulation during myogenesis. It also raises potential clinical implications by suggesting that targeting the Trim32-c-Myc axis, or modulating c-Myc stability, may represent a therapeutic strategy for LGMDR8. This work will be of particular interest to muscle biology researchers studying myogenesis and the molecular basis of muscle disease, RNA biology specialists investigating post-transcriptional regulation and mRNA stability, and neuromuscular disease researchers and clinicians seeking to identify new molecular targets for therapeutic intervention in LGMDR8. * * The Reviewer expressing this opinion is an expert in muscle stem cells, muscle regeneration, and muscle development.

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

Summary: * * In this study, the authors sought to investigate the molecular role of Trim32, a tripartite motif-containing E3 ubiquitin ligase often associated with its dysregulation in Limb-Girdle Muscular Dystrophy Recessive 8 (LGMDR8), and its role in the dynamics of skeletal muscle differentiation. Using a CRISPR-Cas9 model of Trim32 knockout in C2C12 murine myoblasts, the authors demonstrate that loss of Trim32 alters the myogenic process, particularly by impairing the transition from proliferation to differentiation. The authors provide evidence in the way of transcriptomic profiling that displays an alteration of myogenic signaling in the Trim32 KO cells, leading to a disruption of myotube formation in-vitro. Interestingly, while previous studies have focused on Trim32's role in protein ubiquitination and degradation of c-Myc, the authors provide evidence that Trim32-regulation of c-Myc occurs at the level of mRNA stability. The authors show that the sustained c-Myc expression in Trim32 knockout cells disrupts the timely expression of key myogenic factors and interferes with critical withdrawal of myoblasts from the cell cycle required for myotube formation. Overall, the study offers a new insight into how Trim32 regulates early myogenic progression and highlights a potential therapeutic target for addressing the defects in muscular regeneration observed in LGMDR8.

We thank the Reviewer for valuing our work and for their appreciated suggestions to improve our manuscript. We have carefully addressed some of the concerns raised as detailed here, while others, which require more laborious experimental efforts, will be addressed as reported in the Revision Plan.

Major Comments:

The work is a bit incremental based on this:

https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0030445 * * And this:

https://www.nature.com/articles/s41418-018-0129-0 * * To their credit, the authors do cite the above papers.

Authors’ response. We thank the Reviewer for this careful evaluation of our work against the current literature and for recognising the contribution of our findings to the understanding of myogenesis complex picture in which the involvement of Trim32 and c-Myc, and of the Trim32-c-Myc axis, can occur at several stages and likely in narrow time windows along the process, thus possibly explaining some reports inconsistencies.

The authors do provide compelling evidence that Trim32 deficiency disrupts C2C12 myogenic differentiation and sustained c-Myc expression contributes to this defective process. However, while knockdown of c-Myc does restore Myogenin levels, it was not sufficient to normalize myotube morphology or differentiation index, suggesting an incomplete picture of the Trim32-dependent pathways involved. The authors should qualify their claim by emphasizing that c-Myc regulation is a major, but not exclusive, mechanism underlying the observed defects. This will prevent an overgeneralization and better align the conclusions with the author's data.

Authors’ response. We agree with the Reviewer and we modified our phrasing that implied Trim32-c-Myc axis as the exclusive mechanism by explicitly indicated that other pathways contribute to guarantee proper myogenesis, in the Abstract and in Discussion.

The Abstract now reads: “… suggesting that the Trim32–c-Myc axis may represent an essential hub, although likely not the exclusive molecular mechanism, in muscle regeneration within LGMDR8 pathogenesis.”

The Discussion now reads: “Functionally, we demonstrated that c-Myc contributes to the impaired myogenesis observed in Trim32 KO clones, although this is clearly not the only factor involved in the Trim32-mediated myogenic network; realistically other molecular mechanisms can participate in this process as also suggested by our transcriptomic results.”

The authors provide a thorough and well-executed interrogation of cell cycle dynamics in Trim32 KO clones, combining phosphor-histone H3 flow cytometry of DNA content, and CFSE proliferation assays. These complementary approaches convincingly show that, while proliferation states remain similar in WT and KO cells, Trim32-deficient myoblasts fail in their normal withdraw from the cell cycle during exposure to differentiation-inducing conditions. This work adds clarity to a previously inconsistent literature and greatly strengthens the study.

Authors’ response. We thank the Reviewer for appreciating our thorough analyses on cell cycle dynamics in proliferation conditions and at the onset of the differentiation process.

The transcriptomic analysis (detailed In the "Transcriptomic analysis of Trim32 WT and KO clones along early differentiation" section of Results) is central to the manuscript and provides strong evidence that Trim32 deficiency disrupts normal differentiation processes. However, the description of the pathway enrichment results is highly detailed and somewhat compressed, which may make it challenging for readers to following the key biological 'take-homes'. The narrative quickly moves across their multiple analyses like MDS, clustering, heatmaps, and bubble plots without pausing to guide the reader through what each analysis contributes to the overall biological interpretation. As a result, the key findings (reduced muscle development pathways in KO cells and enrichment of cell cycle-related pathways) can feel somewhat muted. The authors may consider reorganizing this section, so the primary biological insights are highlighted and supported by each of their analyses. This would allow the biological implications to be more accessible to a broader readership.

Authors’ response. We thank the Reviewer for raising this point and apologise for being too brief in describing the data, leaving indeed some points excessively implicit. As suggested, we now reorganised this session and added the lists of enriched canonical pathways relative to WT vs KO comparisons at D0 and D3 (Fig. EV3B) as well as those relative to the comparison between D0 and D3 for both WT and Trim32 KO samples (Fig. EV3C), with their relative scores. We changed the Results section “Transcriptomic analysis of Trim32 WT and Trim32 KO clones along early differentiation” as reported here below and modified the legends accordingly.

The paragraph now reads: “Based on our initial observations, the absence of Trim32 already exerts a significant impact by day 3 (D3) of C2C12 myogenic differentiation. To investigate how Trim32 influences early global transcriptional changes during the proliferative phase (D0) and early differentiation (D3), we performed an unbiased transcriptomic profiling of WT and Trim32 KO clones (Fig. 2A). Multidimensional Scaling (MDS) analysis revealed clear segregation of gene expression profiles based on both time of differentiation (Dim1, 44% variance) and Trim32 genotype (Dim2, 16% variance) (Fig. 2A). Likewise, hierarchical clustering grouped WT and Trim32 KO clones into distinct clusters at both timepoints, indicating consistent genotype-specific transcriptional differences (Fig. EV3A). Differentially Expressed Genes (DEGs) were detected in the Trim32 KO transcriptome relative to WT, at both D0 and D3. In proliferating conditions, 72 genes were upregulated and 189 were downregulated whereas at D3 of differentiation, 72 genes were upregulated and 212 were downregulated. Ingenuity Pathway Analysis of the DEGs revealed the top 10 Canonical Pathways displayed in Fig. EV3B as enriched at either D0 or D3 (Fig. EV3B). Several of these pathways can underscore relevant Trim32-mediated functions though most of them represent generic functions not immediately attributable to the observed myogenesis defects.

Notably, the transcriptional divergence between WT and Trim32 KO cells is more pronounced at D3, as evidenced by a greater separation along the MSD Dim2 axis, suggesting that Trim32-dependent transcriptional regulation intensifies during early differentiation (Fig. 2A). Given our interest in the differentiation process, we therefore focused our analyses comparing the changes occurring from D0 to D3 in WT (WT D3 vs. D0) and in Trim32 KO (KO D3 vs. D0) RNAseq data.

Pathway enrichment analysis of D3 vs. D0 DEGs allowed the selection of the top-scored pathways for both WT and Trim32 KO data. We obtained 18 top-scored pathways enriched in each genotype (-log(p-value) ³ 9 cut-off): 14 are shared while 4 are top-ranked only in WT and 4 only in Trim32 KO (Fig. EV3C). For the following analyses, we employed thus a total of 22 distinct pathways and to better mine those relevant in the passage from the proliferation stage to the early differentiation one and that are affected by the lack of Trim32, we built a bubble plot comparing side-by-side the scores and enrichment of the 22 selected top-scored pathways above in WT and Trim32 KO (Fig. 2B). A heatmap of DEGs included within these selected pathways confirms the clustering of the samples considering both the genotypes and the timepoints highlighting gene expression differences (Fig. 2C). These pathways are mainly related to muscle development, cell cycle regulation, genome stability maintenance and few other metabolic cascades.

As expected given the results related to Figure 1, moving from D0 to D3 WT clones showed robust upregulation of key transcripts associated with the Inactive Sarcomere Protein Complex, a category encompassing most genes in the “Striated Muscle Contraction” pathway, while in Trim32 KO clones this pathway was not among those enriched in the transition from D0 to D3 (Fig. EV3C). Detailed analyses of transcripts enclosed within this pathway revealed that on the transition from proliferation to differentiation, WT clones show upregulation of several Myosin Heavy Chain isoforms (e.g., MYH3, MYH6, MYH8), α-Actin 1 (ACTA1), α-Actinin 2 (ACTN2), Desmin (DES), Tropomodulin 1 (TMOD1), and Titin (TTN), a pattern consistent with previous reports, while these same transcripts were either non-detected or only modestly upregulated in Trim32 KO clones at D3 (Fig. 2D). This genotype-specific disparity was further confirmed by gene set enrichment barcode plots, which demonstrated significant enrichment of these muscle-related transcripts in WT cells (FDR_UP = 0.0062), but not in Trim32 KO cells (FDR_UP = 0.24) (Fig. EV3D). These findings support an early transcriptional basis for the impaired myogenesis previously observed in Trim32 KO cells.

In addition to differences in muscle-specific gene expression, we observed that also several pathways related to cell proliferation and cell cycle regulation were more enriched in Trim32 KO cells compared to WT. This suggests that altered cell proliferation may contribute to the distinct differentiation behavior observed in Trim32 KO versus WT (Fig. 2B). Given that cell cycle exit is a critical prerequisite for the onset of myogenic differentiation and considering that previous studies on Trim32 role in cell cycle regulation have reported inconsistent findings, we further examined cell cycle dynamics under our experimental conditions to clarify Trim32 contribution to this process”

The work would be greatly strengthened by the conclusion of LGMDR8 primary cells, and rescue experiments of TRIM32 to explore myogenesis.

Authors’ response. This point will be addressed as detailed in the Revision Plan

Also, EU (5-ethynyl uridine) pulse-chase experiments to label nascent and stable RNA coupled with MYC pulldowns and qPCR (or RNA-sequencing of both pools) would further enhance the claim that MYC stability is being affected.

Authors’ response. This point will be addressed as detailed in the Revision Plan

"On one side, c-Myc may influence early stages of myogenesis, such as myoblast proliferation and initial myotube formation, but it may not contribute significantly to later events such as myotube hypertrophy or fusion between existing myotubes and myocytes. This hypothesis is supported by recent work showing that c-Myc is dispensable for muscle fiber hypertrophy but essential for normal MuSC function (Ham et al, 2025)." Also address and discuss the following, as what is currently written is not entirely accurate: https://www.embopress.org/doi/full/10.1038/s44319-024-00299-z and https://journals.physiology.org/doi/prev/20250724-aop/abs/10.1152/ajpcell.00528.2025

Authors’ response. We thank the Reviewer for bringing to our attention these two publications, that indeed, add important piece of data to recapitulate the in vivo complexity of c-Myc role in myogenesis. We included this point in our Discussion.

The Discussion now reads: “On one side, c-Myc may influence early stages of myogenesis, such as myoblast proliferation and initial myotube formation, but it may not contribute significantly to later events such as myotube hypertrophy or fusion between existing myotubes and myocytes. This hypothesis is supported by recent work showing that c-Myc is dispensable for muscle fiber hypertrophy but essential for normal MuSC function (Ham et al, 2025). Other reports, instead, demonstrated the implication of c-Myc periodic pulses, mimicking resistance-exercise, in muscle growth, a role that cannot though be observed in our experimental model (Edman et al., 2024; Jones et al., 2025).”

Minor Comments:

Z-score scale used in the pathway bubble plot (Figure 2C) could benefit from alternative color choices. Current gradient is a bit muddy and clarity for the reader could be improved by more distinct color options, particularly in the transition from positive to negative Z-score.

Authors’ response. As suggested, we modified the z-score-representing colors using a more distinct gradient especially in the positive to negative transition in Figure 2B.

Clarification on the rationale for selecting the "top 18" pathways would be helpful, as it is not clear if this cutoff was chosen arbitrarily or reflects a specific statistical or biological threshold.

Authors’ response. As now better explained (see comment regarding Major point: Transcriptomics), we used a cut-off of -log(p-value) above or equal to 9 for pathways enriched in DEGs of the D0 vs D3 comparison for both WT and Trim32 KO. The threshold is now included in the Results section and the pathways (shared between WT and Trim32 KO and unique) are listed as Fig. EV3C.

The authors alternates between using "Trim 32 KO clones" and "KO clones" throughout the manuscript. Consistent terminology across figures and text would improve readability.

Authors’ response. We thank the Reviewer for this remark, and we apologise for having overlooked it. We amended this throughout the manuscript by always using for clarity “Trim32 KO clones/cells”.

Cell culture methodology does not specify passage number or culture duration (only "At confluence") before differentiation. This is important, as C2C12 differentiation potential can drift with extended passaging.

Authors’ response. We agree with the Reviewer that C2C12 passaging can reduce the differentiation potential of this myoblast cell lines; this is indeed the main reason why we decided to employ WT clones, which underwent the same editing process as those that resulted mutated in the Trim32 gene, as reference controls throughout our study. We apologise for not indicating the passages in the first version of the manuscript that now is amended as per here below in the Methods section:

“The C2C12 parental cells used in this study were maintained within passages 3–8. All clonal cell lines (see below) were utilized within 10 passages following gene editing. In all experiments, WT and Trim32 KO clones of comparable passage numbers were used to ensure consistency and minimize passage-related variability.”

Reviewer #2 (Significance (Required)):

General Assessment:

This study provides a thorough investigation of Trim32's role the processes related to skeletal muscle differentiation using a CRISPR-Cas9 knockout C2C12 model. The strengths of this study lie in the multi-layered experimental approach as the authors incorporated transcriptomics, cell cycle profiling, and stability assays which collectively build a strong case for their hypothesis that Trim32 is a key factor in the normal regulation of myogenesis. The work is also strengthened by the use of multiple biological and technical replicates, particularly the independent KO clones which helps address potential clonal variation issues that could occur. The largest limitation to this study is that, while the c-Myc mechanism is well explored, the other Trim32-dependent pathways associated with the disruption (implicated by the incomplete rescue by c-Myc knockdown) are not as well addressed. Overall however, the study convincingly identifies a critical function for Trim32 during skeletal muscle differentiation. * * Advance: * * To my knowledge, this is the first study to demonstrate the mRNA stability level of c-Myc regulation by Trim32, rather than through the ubiquitin-mediated protein degradation. This work will advance the current understanding and provide a more complete understanding of Trim32's role in c-Myc regulation. Beyond c-Myc, this work highlights the idea that TRIM family proteins can influence RNA stability which could implicate a broader role in RNA biology and has potential for future therapeutic targeting. * * Audience: * * This research will be of interest to an audience that focuses on broad skeletal muscle biology but primarily to readers with more focused research such as myogenesis and neuromuscular disease (LGMDR8 in particular) where the defined Trim32 governance over early differentiation checkpoints will be of interest. It will also provide mechanistic insights to those outside of skeletal muscle that study TRIM family proteins, ubiquitin biology, and RNA regulation. For translational/clinical researchers, it identifies the Trim32/c-Myc axis as a potential therapeutic target for LGMDR8 and related muscular dystrophies.

Expertise: * * My expertise lies in skeletal muscle biology, gene editing, transgenic mouse models, and bioinformatics. I feel confident evaluating the data and conclusions as presented.

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

• In this paper, the authors examine the role of TRIM32, implicated in limb girdle muscular dystrophy recessive 8 (LGMDR8), in the differentiation of C2C12 mouse myoblasts. Using CRISPR, they generate mutant and wild-type clones and compare their differentiation capacity in vitro. They report that Trim32-deficient clones exhibit delayed and defective myogenic differentiation. RNA-seq analysis reveals widespread changes in gene expression, although few are validated by independent methods. Notably, Trim32 mutant cells maintain residual proliferation under differentiation conditions, apparently due to a failure to downregulate c-Myc. Translation inhibition experiments suggest that TRIM32 promotes c-Myc mRNA destabilization, but this conclusion is insufficiently substantiated. The authors also perform rescue experiments, showing that c-Myc knockdown in Trim32-deficient cells alleviates some differentiation defects. However, this rescue is not quantified, was conducted in only two of the three knockout lines, and is supported by inappropriate statistical analysis of gene expression. Overall, the manuscript in its current form has substantial weaknesses that preclude publication. Beyond statistical issues, the major concerns are: (1) exclusive reliance on the immortalized C2C12 line, with no validation in primary/satellite cells or in vivo, (2) insufficient mechanistic evidence that TRIM32 acts directly on c-Myc mRNA, and (3) overinterpretation of disease relevance in the absence of supporting patient or in vivo data. Please find more details below:*

We thank the Reviewer for the in-depth assessment of our work and precious suggestions to improve the manuscript. We have carefully addressed some of the concerns raised, as detailed here, while others, which require more experimental efforts, will be addressed as detailed in the Revision Plan.

- TRIM32 complementation / rescue experiments to exclude clonal or off-target CRISPR effects and show specificity are lacking.

Authors’ response. This point will be addressed as detailed in the Revision Plan

- The authors link their in vitro findings to LGMDR8 pathogenesis and propose that the Trim32-c-Myc axis may serve as a central regulator of muscle regeneration in the disease. However, LGMDR8 is a complex disorder, and connecting muscle wasting in patients to differentiation assays in C2C12 cells is difficult to justify. No direct evidence is provided that the proposed mRNA mechanism operates in patient-derived samples or in mouse satellite cells. Moreover, the partial rescue achieved by c-Myc knockdown (which does not fully restore myotube morphology or differentiation index) further suggests that the disease connection is not straightforward. Validation of the TRIM32-c-Myc axis in a physiologically relevant system, such as LGMD patient myoblasts or Trim32 mutant mouse cells, would greatly strengthen the claim.

Authors’ response. This point will be addressed as detailed in the Revision Plan

-Some gene expression changes from the RNA-seq study in Figure 2 should be validated by qPCR

Authors’ response. We thank the reviewer for this suggestion. This point will be addressed as detailed in the Revision Plan. We have selected several transcripts that will be evaluated in independent samples in order to validate the RNAseq results.

- The paper shows siRNA knockdown of c-Myc in KO restores Myogenin RNA/protein but does not fully rescue myotube morphology or differentiation index. This suggests that Trim32 controls additional effectors beyond c-Myc; yet the authors do not pursue other candidate mediators identified in the RNA-seq. The manuscript would be strengthened by systematically testing whether other deregulated transcripts contribute to the phenotype.

Authors’ response. This point will be addressed as detailed in the Revision Plan

- There are concerns with experimental/statistical issues and insufficient replicate reporting. The authors use unpaired two-tailed Student's t-test across many comparisons; multiple testing corrections or ANOVA where appropriate should be used. In Figure EV5B and Figure 6B, the authors perform statistical analyses with control values set to 1. This method masks the inherent variability between experiments and artificially augments p values. Control sample values need to be normalized to one another to have reliable statistical analysis. Myotube morphology and differentiation index quantifications need clear description of fields counted, blind analysis, and number of biological replicates.

Authors’ response. We thank the Reviewer for raising this point.

Regarding the replicates, we clarified in the Methods and Legends that the Trim32 KO experiments have been performed on 3 biological replicates (independent clones) and the same for the reference control (3 independent WT clones), except for the Fig. 6 experiments that were performed on 2 Trim32 KO and 2 WT clones. All the Western Blots, immunofluorescence, qPCR data are representative of the results of at least 3 independent experiments unless otherwise stated. We reported the number and type of replicates as well as the microscope fields analyzed.

We repeated the statistical analyses of the data in Figure 5G, EV5D, EV5E, employing more appropriately the 2-way-ANOVA test, as suggested, and we now reported this info in the graphs and legends.

We thank the Reviewer for raising this point, we agree and substituted the graphs in Fig. EV5B and 6B showing the control values normalised as suggested. The statistical analyses now reflect this change.

-Some English mistakes require additional read-throughs. For example: "Indeed, Trim32 has no effect on the stability of c-Myc mRNA in proliferating conditions, but upon induction of differentiation the stability of c-Myc mRNA resulted enhanced in Trim32 KO clones (Fig. 5G, Fig. EV5D and 5E)."

Authors’ response. We re-edited this revised version of the manuscript as suggested.

-Results in Figure 5A should be quantified

Authors’ response. We amended this point by quantifying the results shown in Fig. 5A, we added the graph of the quantification of 3 experimental replicates to the Figure. Quantification confirms that no statistically significant difference is observed. The Figure and the relative legend are modified accordingly.

-Based on the nuclear marker p84, the separation of cytoplasmic and nuclear fractions is not ideal in Figure 5D

Authors’ response. We agree with the Reviewer that the presence of p84 also in the cytoplasmic fraction is not ideal. Regrettably, we observed this faint p84 band in all the experiments performed. We think however, that this is not impacting on the result that clearly shows that c-Myc and Trim32 are never detected in the same compartment.

-In Figure 6, it is not appropriate to perform statistical analyses on only two data points per condition.

Authors’ response. We agree with the Reviewer and we now show the graph of the results of the 3 technical replicates for 2 biological replicates and do not indicate any statistics (Fig. 6B). The graph was also modified according to a previous point raised.

-The nuclear MYOG phenotype is very interesting; could this be related to requirements of TRIM32 in fusion?

Authors’ response. We agree with the Reviewer that Trim32 might also be necessary for myoblast fusion. This point is however beyond the scope of the present study and will be addressed in future work.

- The hypothesis that TRIM32 destabilizes c-Myc mRNA is intriguing but requires stronger mechanistic support. This would be more convincing with RNA immunoprecipitation to test direct association with c-Myc mRNA, and/or co-immunoprecipitation to identify interactions between TRIM32 and proteins involved in mRNA stability. The study would also be strengthened by reporter assays, such as c-Myc 3′UTR luciferase constructs in WT and KO cells, to directly demonstrate 3′UTR-dependent regulation of mRNA stability.

Authors’ response. This point will be addressed as detailed in the Revision Plan

Reviewer #3 (Significance (Required)):

The manuscript presents a minor conceptual advance in understanding TRIM32 function in myogenic differentiation. Its main limitation is that all experiments were performed in C2C12 cells. While C2C12 are a classical system to study muscle differentiation, they are an immortalized, long-cultured, and genetically unstable line that represents a committed myoblast stage rather than bona fide satellite cells. They therefore do not fully model the biology of early regenerative responses. Several TRIM32 phenotypes reported in the literature differ between primary satellite cells and cell lines, and the authors themselves note such discrepancies. Extrapolating these findings to LGMDR8 pathogenesis without validation in primary human myoblasts, satellite cell assays, or in vivo regeneration models is therefore not justified. Previous work has already established clear roles for TRIM32 in mouse satellite cells in vivo and in patient myoblasts in vitro, whereas this study introduces a novel link to c-Myc regulation during differentiation. In addition, without mechanistic evidence, the central claim that TRIM32 regulates c-Myc mRNA stability remains descriptive and incomplete. Nevertheless, the results will be of interest to researchers studying LGMD and to those exploring TRIM32 biology in broader contexts. I review this manuscript as a muscle biologist with expertise in satellite cell biology and transcriptional regulation.

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

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

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

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

Author response:

The following is the authors’ response to the previous reviews.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Conceptually, I feel that the authors addressed many concerns. However, I am still not convinced that their data support the strength of their claims. Additionally, I spent considerable time investigating the now freely available code and data and found several inconsistencies that would be critical to rectify. My comments are split into two parts, reflecting concerns related to the responses/methods and concerns resulting from investigation of the provided code/data. The former is described in the public review above. Because I show several figures to illustrate some key points for the latter part, an attached file will provide the second part: https://elife-rp.msubmit.net/elife-rp_files/2025/02/24/00136468/01/136468_1_attach_15_2451_convrt.pdf

(1) This point is discussed in more detail in the attached file, but there are some important details regarding the identification of the learned trial that require more clarification. For instance, isn’t the original criterion by Gibbon et al. (1977) the first “sequence of three out of four trials in a row with at least one response”? The authors’ provided code for the Wilcoxon signed rank test and nDkl thresholds looks for a permanent exceeding of the threshold. So, I am not yet convinced that the approaches used here and in prior papers are directly comparable.

We agree that there remain unresolved issues with our two attempts to create criteria that match that used by Gibbon and Balsam for trials to criterion. Therefore, we have decided to remove those analyses and return to our original approach showing trials to acquisition using several different criteria so as to demonstrate that the essential feature of the results—the scaling between learning rate and information—is robust. Figure 2A shows the results for a criterion that identifies the trial after which the cumulative response rate during the CS (=cumulative CS response count from Trial 1 divided by cumulative CS time from Trial 1) is consistently above the cumulative overall response rate across the trial (i.e., including both the CS and ITI). These data compare the CS response rate with the overall response rate, rather than with ITI rate as done in the previous version (in Figure 3A of that submission), to be consistent with the subsequent comparisons that are made using the nDkl. (The nDkl relies on the comparison between the CS rate and the overall rate, rather than between the CS and ITI rates.) Figures 2B and 2C show trials to acquisition when two statistical criteria, based on the nDkl, are applied to the difference between CS and overall response rates (the criteria are for odds >= 4:1 and p<.05). As we now explain in the text, a statistical threshold is useful inasmuch as it provides some confidence to the claim that the animals had learned by a given trial. However, this trial is very likely to be after the point when they had learned because accumulating statistical evidence of a difference necessarily adds trials.

Also, there’s still no regression line fitted to their data (Fig 3’s black line is from Fig 1,according to the legends). Accordingly, I think the claim in the second paragraph of the Discussion that the old data and their data are explained by a model with “essentially the same parameter value” is not yet convincing without actually reporting the parameters of the regression. Related to this, the regression for their data based on my analysis appears to have a slope closer to -0.6, which does not support strict timescale invariance. I think that this point should be discussed as a caveat in the manuscript.

We now include regression lines fitted to our data in Figures 2A-C, and their slopes are reported in the figure note. We also note on page 14 of the revision that these regressions fitted to our data diverge from the black regression line (slope -1) as the informativeness increases. On pages 14-15, we offer an explanation for this divergence; that, in groups with high informativeness, the effective informativeness is likely to be lower than the assigned value because the rats had not been magazine trained which means they would not have discovered the food pellet as soon as it was released on the first few trials. On pages 15-16, we go on to note that evidence for a change in response rate during the CS in those very first few trials may have been missed because the initial response rates were very low in rats trained with very long inter-reinforcement intervals (and thus high informativeness). We also propose a solution to this problem of comparing between very low response rates, one that uses the nDkl to parse response rates into segments (clusters of trials with equivalent response rates). This analysis with parsed response rates provides evidence that differential responding to the CS may have been acquired earlier than is revealed using trial-by-trial comparisons.

(2) The authors report in the response that the basis for the apparent gradual/multiple step-like increases after initial learning remains unclear within their framework. This would be important to point out in the actual manuscript Further, the responses indicating the fact that there are some phenomena that are not captured by the current model would be important to state in the manuscript itself.

We have included a paragraph (on page 26) that discusses the interpretation of the steady/multi-step increase in responding across continued training.

(3) There are several mismatches between results shown in figures and those produced by the authors’ code, or other supplementary files. As one example, rat 3 results in Fig 11 and Supplementary Materials don’t match and neither version is reproduced by the authors’ code. There are more concerns like this, which are detailed in the attached review file.

Addressed next….

The following is the response to the points raised in Part 2 of Reviewer 1’s pdf.

(1a) I plotted the calculated nDkl with the provided code for rat 3 (Fig 11), but itlooks different, and the trials to acquisition also didn’t match with the table  provided (average of ~20 trial difference). The authors should revise the provided code and plots. Further, even in their provided figures, if one compares rat 3 in Supplementary Materials to data from the same rat in Fig 11, the curves are different. It is critical to have reproducible results in the manuscript, including the ability to reproduce with the provided code.

We apologise for those inconsistencies. We have checked the code and the data in the figures to ensure they are all now consistent and match the full data in the nHT.mat file in OSF. Figures 11 and 12 from the previous version are now replaced with Figure 6 in the revised manuscript (still showing data from Rats 3 and 176). The data plotted in Fig 6 match what is plotted in the supplementary figures for those 2 rats (but with slightly different cropping of the x-axes) and all plots draw directly from nHT.mat.

(1b) I tried to replicate also Fig 3C with the results from the provided code, but I failed especially for nDkl > 2.2. Fig 3A and B look to be OK.

There was error in the previous Fig 3C which was plotting the data from the wrong column of the Trials2Acquisition Table. We suspect this arose because some changes to the file were not updated in Dropbox. However, that figure has changed (now Figure 2) as already mentioned, and no longer plots data obtained with that specific nDkl criterion. The figure now shows criteria that do not attempt to match the Gibbon and Balsam criterion.

(1c) The trials to learn from the code do match with those in the  Trials2Acquisition Table, but the authors’ code doesn’t reproduce the reported trials to learn values in the nDkl Acquisition Table. The trials to learn from the code are ~20 trials different on average from the table’s ones, for 1:20, 1:100, and 1:1000 nDkl.

We agree that discrepancies between those different files were a source of potential confusion because they were using different criteria or different ways of measuring response rate (i.e., the “conventional” calculation of rate as number of responses/time, vs our adjusted calculation in which the 1^st response in the CS was excluded as well as the time spent in the magazine, vs parsed response rates based on inter-response intervals). To avoid this, there is now a single table called Acquisition_Table.xlsx in OSF that includes Trials to acquisition for each rat based on a range of criteria or estimates of response rate in labelled columns. The data shown in Figure 2 are all based on the conventional calculation of response rate (provided in Columns E to H of Acquisition_Table.xlsx). To make the source of these data explicit, we have provided in OSF the matlab code that draws the data from the nHT.mat file to obtain these values for trials-to-acquisition.

(1d) The nDkl Acquisition Table has columns with the value of the nDkl statistics at various acquisition landmarks, but the value does not look to be true, especially for rat 19. The nDkl curve provided by the authors (Supplementary Materials) doesn’t match the values in the table. The curve is below 10 until at least 300 trials, while the table reports a value higher than 20 (24.86) at the earliest evidence of learning (~120 trials?).

We are very grateful to the reviewer for finding this discrepancy in our previous files. The individual plots in the Supplementary Materials now contain a plot of the nDkl computed using the conventional calculation of response rate (plot 3 in each 6-panel figure) and a plot of the nDkl computed using the new adjusted calculation of response rate (plot 4). These correspond to the signed nDkl columns for each rat in the full data file nHT.mat. The nDkl values at different acquisition landmarks included in Acquisition_Table.xlsx (Cols AB to AF) correspond to the second of these nDkl formulations. We point out that, of the acquisition landmarks based on the conventional calculation of response rate (Cols E to J of Acquisition_Tabls.xlsx), only the first two landmarks (CSrate>Contextrate and min_nDkl) match the permanently positive and minimum values of the plotted nDkl values. This is because the subsequent acquisition landmarks are based on a recalculation of the nDkl starting from the trial when CSrate>ContextRate, whereas the plotted nDkl starts from Trial 1.

(2) The cumulative number of responses during the trial (Total) in the raw data table is not measured directly, but indirectly estimated from the pre-CS period, as (cumNR_Pre*[cumITI/cumT_Pre])+ cumNR_CS (cumNR_Pre: cumulative nose-poke response number during pre-CS period; cumITI: cumulative sum of ITI duration; cumT_Pre: cumulative pre-CS duration; cumNR_CS: cumulative response number during CS), according to ‘Explanation of TbyTdataTable (MATLAB).docx’.Why not use the actual cumulative responses during the whole trial instead of using a noisier measure during a smaller time window and then scaling it for the total period?

Unfortunately, the bespoke software used to control the experimental events and record the magazine activity did not record data continuously throughout the experiment. The ITI responses were only sampled during a specified time-window (the “pre-CS” period) immediately before each CS onset. Therefore, response counts across the whole ITI had to be extrapolated.

(3) Regarding the “Matlab code for Find Trials to Criterion.docx”:

(a) What’s the rationale for not using all the trials to calculate nDkl but starting the cumulative summation from the earliest evidence trial (truncated)? Also, this procedure is not described in the manuscript, and this should be mentioned.

The procedure was perhaps not described clearly enough in the previous manuscript. We have expanded that text to make it clearer (page 12) which includes the text…

“We started from this trial, rather than from Trial 1, because response rate data from trials prior to the point of acquisition would dilute the evidence for a statistically significant difference in responding once it had emerged, and thereby increase the number of trials required to observe significant responding to the CS. The data from Rat 1 illustrates this point. The CS response rate of Rat 1 permanently exceeded its overall response rate on Trial 52 (when the nD_KL also became permanently positive). The nD_KL, calculated from that trial onwards, surpassed 0.82 (odds 4:1) after a further 11 trials (on Trial 63) and reached 1.92 (p < .05) on Trial 81. By contrast, the nD_KL for this rat, calculated from Trial 1, did not permanently exceed 0.82 until Trial 83 and did not exceed 1.92 until Trial 93, adding 10 or 20 trials to the point of acquisition.”

(3b) The authors' threshold is the trial when the nDkl value exceeds the threshold permanently.  What about using just the first pass after the minimum?

Rat 19 provides one example where the nDkl was initially positive, and even exceeded threshold for odds 4:1 and p<.05, but was followed by an extended period when the nDkl was negative because the CS response rate was less than the overall response rate. It illustrates why the first trial on which the nDkl passes a threshold cannot be used as a reliably index of acquisition.

(3c) Can the authors explain why a value of 0.5 is added to the cumulative response number before dividing it by the cumulative time?

This was done to provide an “unbiased” estimate of the response count because responses are integers. For example, if a rat has made 10 responses over 100 s of cumulative CS time, the estimated rate should be at least 10/100 but could be anything up to, but not including, 11/100. A rate of 10.5/100 is the unbiased estimate. However, we have now removed this step when calculating the nDkl to identify trials to acquisition because we recognise that it would represent a larger correction to the rate calculated across short intervals than across long intervals and therefore bias comparison between CS and overall response rates that involve very different time durations. As such, the correction would artefactually inflate evidence that the CS response rate was higher than the contextual response rate. However, as noted earlier in this reply, we have now instituted a similar correction when calculating the pre-CS response rate over the final 5 sessions for rats that did not register a single response (hence we set their response count to 0.5).

(3d) Although the authors explain that nDkl was set to negative if pre-CS rate is higher than CS rate, this is not included in the code because the code calculates the nDkl using the truncated version, starting to accumulate the poke numbers and time from the earliest evidence, thus cumulative CS rate is always higher than cumulative contextual rate. I expect then that the cumulative CS rate will be always higher than the cumulative pre-CS rate.

Yes, that is correct. The negative sign is added to the nDkl when it is computed starting from Trial 1. But when it is computed starting from the trial when the CS rate is permanently > the overall rate, there is no need to add a sign because the divergence is always in the positive direction.

(3e) Regarding the Wilcoxon signed rank test, please clarify in the manuscript that the input ‘rate’ is not the cumulative rate as used for the earliest evidence. Please also clarify if the rates being compared for the signed nDkl are just the instantaneous rates or the cumulative ones. I believe that these are the ‘cumulative’ ones (not as for Wilcoxon signed rank test), because if not, the signed nDkl curve of rat 3 would fluctuate a lot across the x-axis.

The reviewer is correct in both cases. However, as already mentioned, we have removed the analysis involving the Wilcoxon test. The description of the nDkl already specifies that this was done using the cumulative rates.

(4) Supplemental table ‘nDkl Acquisition Table.xlsx’ 3rd column (“Earliest”) descriptions are unclear.

(a) It is described in the supplemental ‘Explanation of Excel Tables.docx’ as the ‘earliest estimate of the onset of a poke rate during the CSs higher than the contextual poke rate’, while the last paragraph of the manuscript’s method section says ‘Columns 4, 5 and 6 of the table give the trial after which conditioned responding appeared as estimated in the above described three different ways— by the location of the minimum in the nDkl, the last upward 0 crossings, and the CS parse consistently greater than the ITI parse, respectively. Column 3 in that table gives the minimum of the three estimates.’ I plotted the data from column 3 (right) and comparing them with Fig 3A (left) makes it clear that there’s an issue in this column. If the description in the ‘Explanation of Excel Tables.docx’ is incorrect, please update it.

We agree that the naming of these criteria can cause confusion, hence we have changed them. On page 9 we have replaced “earliest” with “first” in describing the criterion plotted in Figure 2A showing the trial starting from which the cumulative CS response rate permanently exceeded the cumulative overall rate. What is labelled as “Earliest” in “Acquisition_Table.xlsx” is, as the explanation says, the minimum value across the 3 estimates in that table.

(b) Also, the term ‘contextual poke rate’ in the 3rd column’s description isconfusing as in the nDkl calculation it represents the poke rate during all the training time, while in the first paragraph of the ‘Data analysis’ part, the earliest evidence is calculated by comparing the ITI (pre-CS baseline) poke rate.

Yes, we have kept the term “contextual” response rate to refer to responding across the whole training interval (the ITI and the CS duration). This is used in calculation of the nDkl. For consistency with this comparison, we now take the first estimate of acquisition (in Fig 2A) based on a comparison between the CS rate and the overall (context) rate (not the pre-CS rate).

Reviewer #2 (Recommendations for the authors):

In response to the Rebuttal comments:

Analytical (1) relating to Figure 3C/D

This is a reasonable set of alternative analyses, but it is not clear that it answers the original comment regarding why the fit was worse when using a theoretically derived measure. Indeed, Figure 3C now looks distinctly different to the original Gibbon and Balsam data in terms of the shape of the relationship (specifically, the Group Median - filled orange circles) diverge from the black regression line.

As mentioned in response to Reviewer 1, there was a mistake in Figure 3C of the revised manuscript. The figure was actually plotting data using a more stringent criterion of nDkl > 5.4, corresponding to p<0.001. The figure was referencing the data in column J of the public Trials2Acquisition Table. The data previously plotted in Figure 3C are no longer plotted because we no longer attempt to identify a criterion exactly matching that used by Gibbon and Balsam.

We agree that the data shown in the first 3 panels of Figure 2 do diverge somewhat from the black regression line at the highest levels of informativeness (C/T ratios > 70), and the regression lines fitted to the data have slopes greater than -1. We acknowledge this on page 14 of the revised manuscript. Since Gibbon and Balsam did not report data from groups with such high ratios, we can’t know whether their data too would have diverged from the regression line at this point. We now report in the text a regression fitted to the first 10 groups in our experiment, which have C/T ratios that coincide with those of Gibbon and Balsam, and those regression lines do have slopes much closer to -1 (and include -1 in the 95% confidence intervals). We believe the divergence in our data at the high C/T ratios may be due to the fact that our rats were not given magazine training before commencing training with the CS and food. Because of this, it is quite likely that many rats did not find the food immediately after delivery on the first few trials. Indeed, in subsequent experiments, when we have continued to record magazine entries after CS-offset, we have found that rats can take 90 s or more to enter the magazine after the first pellet delivery. This delay would substantially increase the effective CS-US interval, measured from CS onset to discovery of the food pellet by the rat, making the CS much less informative over those trials. We now make this point on pages 14-15 of the revised manuscript.

Analytical (2)

We may have very different views on the statistical and scientific approaches here.

This scalar relationship may only be uniquely applicable to the specific parameters of an experiment where CS and US responding are measured with the same behavioral response (magazine entry). As such, statements regarding the simplicity of the number of parameters in the model may simply reflect the niche experimental conditions required to generate data to fit the original hypotheses.

To the extent that our data are consistent with the data reported decades ago by Gibbon and Balsam indicates the scalar relationship they identified is not unique to certain niche conditions since those special conditions must be true of both the acquisition of sign-tracking responses in pigeons and magazine entry responses in rats. How broadly it applies will require further experimental work using different paradigms and different species to assess how the rate of acquisition is affected across a wide range of informativeness, just as we have done here.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):           

Summary:

The authors have created a new model of KCNC1-related DEE in which a pathogenic patient variant (A421V) is knocked into a mouse in order to better understand the mechanisms through which KCNC1 variants lead to DEE.  

Strengths:

(1)  The creation of a new DEE model of KCNC1 dysfunction. 

(2)  In Vivo phenotyping demonstrates key features of the model such as early lethality and several types of electrographic seizures. 

(3)  The ex vivo cellular electrophysiology is very strong and comprehensive including isolated patches to accurately measure K+ currents, paired recording to measure evoked synaptic transmission, and the measurement of membrane excitability at different time points and in two cell types.

We thank Reviewer 1 for these positive comments related to strengths of the study.   

Weaknesses:

(1) The assertion that membrane trafficking is impaired by this variant could be bolstered by additional data.

We agree with this comment. However, given the technical challenges of standard biochemical experiments for investigating voltage-gated potassium channels (e.g., antibody quality), the lack of a Kv3.1-A421V specific antibody, and the fact that Kv3.1 is expressed in only a small subset of cells, we did not undertake this approach. However, we did perform additional experiments and analysis to improve the rigor of the experiments supporting our conclusion that membrane trafficking is impaired in the Kcnc1-A421V/+ mouse. 

Such experiments support a highly significant and robust difference in our (albeit imperfect) measurement of the membrane:cytosol ratio of Kv3.1 immunofluorescence between WT and Kcnc1-A421V/+ mice, which is consistent with lack of membrane trafficking (Figure 3). In the revised manuscript, we have added additional data points to this plot and updated the representative example images using improved imaging techniques to better showcase how Kcnc1-A421V/+ PV-INs differ from age-matched WT littermate controls. We think the result is quite clear. Future biochemical experiments perhaps best performed in a culture system in vitro could provide additional support for this conclusion.

(2) In some experiments details such as the age of the mice or cortical layer are emphasized, but in others, these details are omitted.

We apologize for this omission. We have now clarified the age of the mice and cortical layer for each experiment in the Methods and Results sections as well as figure legends.   

(3) The impairments in PV neuron AP firing are quite large. This could be expected to lead to changes in PV neuron activity outside of the hypersynchronous discharges that could be detected in the 2-photon imaging experiments, however, a lack of an effect on PV neuron activity is only loosely alluded to in the text. A more formal analysis is lacking. An important question in trying to understand mechanisms underlying channelopathies like KCNC1 is how changes in membrane excitability recorded at the whole cell level manifest during ongoing activity in vivo. Thus, the significance of this work would be greatly improved if it could address this question.

Yes, the impairments in the neocortical PV-IN excitability are notably severe relative to other PV interneuronopathies that we and others have directly investigated (e.g., Kv3.1 or Kv3.2-/- knockout mice; Scn1a+/- mice). In the revised version of the manuscript, we have now added a more thorough in vivo 2P calcium imaging investigation and analysis of our in vivo 2P calcium imaging data of PV-IN (and presumptive excitatory cell) neural activity (Figure 8 and Supplementary Figure 9, Methods- lines 230-271 Results- lines 630-657, and Discussion lines- 795-814). 

Because of the prominent recruitment of neuropil during presumptive myoclonic seizures, further investigation of individual neuronal excitability in vivo required a slightly different labeling strategy now using a soma-tagged GCaMP8m as well as a separate AAV containing tdTomato driven by the PV-IN-specific S5E2 enhancer. Our new results reveal an increase in the baseline calcium transient frequency in non-PV-INs, and reduced mean transient amplitudes in both non-PV cells and PV-INs. These interesting findings, which are consistent with attenuated PV-IN-mediated perisomatic inhibition leading to disinhibited excitatory cells in the Kcnc1-A421V/+ mice, link our in vivo results to the slice electrophysiology experiments. Of course, there are residual issues with the application of this technique to interneurons and the ability to resolve individual or small numbers of spikes, which likely explains the lack of genotype difference in calcium transient frequency in PV-INs.

(4) Myoclonic jerks and other types of more subtle epileptiform activity have been observed in control mice, but there is no mention of littermate control analyzed by EEG. 

We performed additional experiments as requested and did not observe myoclonic jerks or any other epileptic activity in WT control mice. We have included this data in the revised manuscript (Figure 9C).   

Reviewer #2 (Public review):           

Summary:

Wengert et al. generated and thoroughly characterized the developmental epileptic encephalopathy phenotype of Kcnc1A421V/+ knock-in mice. The Kcnc1 gene encodes the Kv3.1 channel subunit. Analogous to the role of BK channels in excitatory neurons, Kv3 channels are important for the recurrent high-frequency discharge in interneurons by accelerating the downward hyperpolarization of the individual action potential. Various Kcnc1 mutations are associated with developmental epileptic encephalopathy, but the effect of a recurrent A421V mutation was somewhat controversial and its influence on neuronal excitability has not been fully established. In order to determine the neurological deficits and underlying disease mechanisms, the authors generated cre-dependent KI mice and characterized them using neonatal neurological examination, high-quality in vitro electrophysiology, and in vivo imaging/electrophysiology analyses. These analyses revealed excitability defects in the PV+ inhibitory neurons associated with the emergence of epilepsy and premature death. Overall, the experimental data convincingly support the conclusion.

Strengths:

The study is well-designed and conducted at high quality. The use of the Cre-dependent KI mouse is effective for maintaining the mutant mouse line with premature death phenotype, and may also minimize the drift of phenotypes which can occur due to the use of mutant mice with minor phenotype for breeding. The neonatal behavior analysis is thoroughly conducted, and the in vitro electrophysiology studies are of high quality.

We appreciate these positive comments from Reviewer 2. 

Weaknesses:

While not critically influencing the conclusion of the study, there are several concerns.

In some experiments, the age of the animal in each experiment is not clearly stated. For example, the experiments in Figure 2 demonstrate impaired K+ conductance and membrane localization, but it is not clear whether they correlated with the excitability and synaptic defects shown in subsequent figures. Similarly, it is unclear how old mice the authors conducted EEG recordings, and whether non-epileptic mice are younger than those with seizures. 

We have now updated the manuscript to include clear report of age for all experiments including the impaired K⁺ conductance (now Figure 3) and EEG (now Figure 9). There was no intention to omit this information. The recordings of K⁺ conductance impairments in PV-INs from Kcnc1-A421V/+ mice were completed at P1621. Thus, we interpret the loss of potassium current density to be causally linked with the impairments in intrinsic physiological function at that same time-period in neocortical layer II-IV PV-INs and more subtly in PV-positive cells in the RTN and neocortical layer V PVINs.

Mice used in the EEG experiments were P24-48, an age range which roughly corresponded with the midpoint on the survival curve for Kcnc1-A421V/+ mice. Although we saw significant mouse-to-mouse variability in seizure phenotype, no Kcnc1-A421V/+ mice completely lacked epilepsy or marked epileptiform abnormalities, neither of which were seen in WT mice. We did not detect a clear relationship between seizure frequency/type and mouse age. 

The trafficking defect of mutant Kv3.1 proposed in this study is based only on the fluorescence density analysis which showed a minor change in membrane/cytosol ratio. It is not very clear how the membrane component was determined (any control staining?). In addition to fluorescence imaging, an addition of biochemical analysis will make the conclusion more convincing (while it might be challenging if the Kv3.1 is expressed only in PV+ cells).

This relates to comment 3 of Reviewer 1. We agree that, in the initial submission of the manuscript, the evidence from IHC for Kv3.1 trafficking deficits was somewhat subtle. In the revised version of the paper, we have gathered additional replicates of this original experiment with improved imaging quality and clarify how the membrane component was specified, to now show a robust and highly significant (***P<0.001) decrease in membrane:cytosol Kv3.1 ratio. We have also now provided new example images better showcasing the deficits observed in the Kcnc1-A421V/+ mice (Figure 3). The membrane compartment was defined as the outermost 1 micron of the parvalbumin-defined cell soma (drawn blind to the Kv3.1b signal), and, importantly, all analysis was conducted blinded to mouse genotype. These measures help to ensure that the result is robust and unbiased. Nonetheless, we have added a paragraph in the Discussion section highlighting the limitations of our IHC evidence for trafficking impairment (Lines 868-883). 

While the study focused on the superficial layer because Kv3.1 is the major channel subunit, the PV+ cells in the deeper cortical layer also express Kv3.1 (Chow et al., 1999) and they may also contribute to the hyperexcitable phenotype via negative effect on Kv3.2; the mutant Kv3.1 may also block membrane trafficking of Kv3.1/Kv3.2 heteromers in the deeper layer PV cells and reduce their excitability. Such an additional effect on Kv3.2, if present, may explain why the heterozygous A421V KI mouse shows a more severe phenotype than the Kv3.1 KO mouse (and why they are more similar to Kv3.2 KO). Analyzing the membrane excitability differences in the deep-layer PV cells may address this possibility.

We appreciate this thoughtful suggestion. We have now provided data from neocortical layer V PV interneurons in the revised manuscript (Supplementary Figure 5). Abnormalities in intrinsic excitability from neocortical layer V PV-INs in Kcnc1A421V/+ mice were present, but less pronounced than in PV-INs from more superficial cortical layers. These results are consistent with the view that greater relative expression of Kv3.2 “dilutes” the impact of the Kv3.1 A421V/+ variant. More specific determination of whether the A421V/+ variant impairs membrane trafficking and/or gating of Kv3.2 remains unclear. 

We attempted to assess how the mutant Kv3.1 affects Kv3.2 localization, but were unsuccessful due to the lack of reliable antibodies. After immunostaining mouse brain sections with two different anti-Kv3.2 antibodies, only one produced somewhat promising signal (see below). However, even in this case, Kv3.2 staining was successful only once (out of five independent staining experiments) and the signal varied across cortical regions, showing widespread cellular Kv3.2 signal in some areas (b, top panel), and barely detectable signal in others, regardless of Kv3.1 expression. In the remaining four attempts, we detected only ‘fiber-like’ immunostaining signal, further diminishing our confidence in anti-Kv3.2 antibody, although results could be improved with still further testing and refinement which we will attempt. Consequently, this important question remains unsolved in this study. 

Author response image 1.

Immunostaining of Kv3.1 and Kv3.2 in sagittal mouse brain sections. a) An example of intracellular Kv3.2 immunostaining signal, variable across the cortex of a WT mice independent of Kv3.1 expression b) Kv3.2 is detectable intracellularly in most of the cells in the top panel but barely detectable in the lowest panel. c) Representative image of Kv3.2 immunostaining signal in other sagittal mouse brain sections.

We have discussed these important implications and limitations of our results in the Discussion (Lines 868-883). We agree with the Reviewer’s interpretation that an impact on Kv3.1/Kv3.2 heteromultimers across the neocortex may explain why the Kcnc1A421V/+ mouse exhibits a more severe phenotype than Kv3.1-/- or Kv3.2-/- mice (see below), a view which we have attempted to further clarify in the Conclusion.    

In Table 1, the A421V PV+ cells show a depolarized resting membrane potential than WT by ~5 mV which seems a robust change and would influence the circuit excitability. The authors measured firing frequency after adjusting the membrane voltage to -65mV, but are the excitability differences less significant if the resting potential is not adjusted? It is also interesting that such a membrane potential difference is not detected in young adult mice (Table 2). This loss of potential compensation may be important for developmental changes in the circuit excitability. These issues can be more explicitly discussed.

We do not entirely understand this finding and its apparent developmental component. It could be compensatory, as suggested by the Reviewer; however, it is transient and seems to be an isolated finding (i.e., it is not accompanied by compensation in other properties). It is also possible that this change in Kcnc1-A421V/+ PV-INs may reflect impaired/delayed development. We cannot test excitability at a meaningfully later time point as the mice are deceased.

The revised version of the manuscript contains additional data (Supplementary Figure 4) showing that major deficits in intrinsic excitability are still observed even when the resting membrane potential is left unadjusted. These results are further discussed in the Results section (lines 522-523) and the Discussion section (lines 727-731).   

Reviewer #3 (Public review):           

Summary:

Here Wengert et al., establish a rodent model of KCNC1 (Kv3.1) epilepsy by introducing the A421V mutation. The authors perform video-EEG, slice electrophysiology, and in vivo 2P imaging of calcium activity to establish disease mechanisms involving impairment in the excitability of fast-spiking parvalbumin (PV) interneurons in the cortex and thalamic PV cells.

Outside-out nucleated patch recordings were used to evaluate the biophysical consequence of the A421V mutation on potassium currents and showed a clear reduction in potassium currents. Similarly, action potential generation in cortical PV interneurons was severely reduced. Given that both potassium currents and action potential generation were found to be unaffected in excitatory pyramidal cells in the cortex the authors propose that loss of inhibition leads to hyperexcitability and seizure susceptibility in a mechanism similar to that of Dravet Syndrome.  

Strengths: 

This manuscript establishes a new rodent model of KCNC1-developmental and epileptic encephalopathy. The manuscript provides strong evidence that parvabumin-type interneurons are impaired by the A421V Kv3.1 mutation and that cortical excitatory neurons are not impaired. Together these findings support the conclusion that seizure phenotypes are caused by reduced cortical inhibition.

We thank Reviewer 3 for their view of the strengths of the study.

Weaknesses:

The manuscript identifies a partial mechanism of disease that leaves several aspects unresolved including the possible role of the observed impairments in thalamic neurons in the seizure mechanism. Similarly, while the authors identify a reduction in potassium currents and a reduction in PV cell surface expression of Kv3.1 it is not clear why these impairments would lead to a more severe disease phenotype than other loss-of-function mutations which have been characterized previously. Lastly, additional analysis of videoEEG data would be helpful for interpreting the extent of the seizure burden and the nature of the seizure types caused by the mutation.

We agree with this comment(s) from Reviewer 3. We studied neurons in the reticular thalamus and layer V neocortical PV-INs since they are also linked to epilepsy pathogenesis and are known to express Kv3.1. However, for most of the study, we focused on neocortical layer II-IV PV-INs, because these cells exhibited the most robust impairments in intrinsic excitability. Cross of our novel Kcnc1-Flox(A421V)/+ mice to a cerebral cortex interneuron-specific driver that would avoid recombination in the thalamus, such as Ppp1r2-Cre (RRID:IMSR_JAX:012686), could assist in determining the relative contribution of thalamic reticular nucleus dysfunction to overall phenotype as used by (Makinson et al., 2017) to address a similar question; however, we have been unable to obtain this mouse despite extensive effort. There are of course other Kv3.1expressing neurons in the brain, including in the hippocampus, amygdala, and cerebellum, and we have provided additional discussion (Lines 731-736) of this issue.

We further agree with the Reviewer that a major question in the field of KCNC1-related neurological disorders is the mechanistic underpinning of why the KCNC1-A421V variant leads to a more severe disease phenotype than other loss of function KCNC1 variants, and, further, why the mouse phenotype is more severe than the Kcnc1 knockout. Previous results and our own recordings in heterologous systems suggest that the A421V variant is more profoundly loss of function than the R320H variant (Oliver et al., 2017; Cameron et al., 2019; Park et al., 2019), which is consistent with A421V having a more severe disease phenotype. Relative to knockout of Kv3.1, our results are consistent with the view that the A421V exhibits dominant negative activity by reducing surface expression of Kv3.1 and/or Kv3.2 (an effect that would not occur in knockout mice), with a possible additional contribution of impairing gating of those Kv3.1-A421V variant containing Kv3.1/Kv3.2 heteromultimers by inclusion of A421V subunits into the heterotetramer. Our finding that the magnitude of total potassium current was reduced in PV-INs by ~50% is consistent with a combination of these various mechanisms but does not distinguish between them.

In the revised version of the manuscript, we have provided a more complete discussion of these important remaining questions regarding our interpretation of how the severity of KCNC1 disorders relates to the biophysical features of the ion channel variant (lines 868883).

Recommendations for the authors

Reviewer #1 (Recommendations for the authors):          

Major

(1) The authors suggest that the reduced K+ current density in Kcnc1-A421V/+ neurons is due in part to impaired trafficking and cell surface expression of Kv3.1 in these neurons. The data supporting this claim aren't completely convincing. First, it's difficult to visualize a difference in Kv3.1 localization in the images shown in panel H, and importantly, it seems problematic that the method to assess Kv3.1 levels in membrane vs. cytosol relied on using PV co-staining to define the membrane compartment as the outermost 1 um of the PV-defined cell soma. This doesn't seem to be the best method to define the membrane compartment, as the PV signal should be largely cytosolic.

As noted above, we have completed additional data collection to confirm our results, and have performed additional imaging and updated our example images to be more representative of the observed deficits in membrane Kv3.1 expression in the Kcnc1-A421V/+ mice. We attempted to identify a marker to more clearly label the membrane to combine with PV immunocytochemistry but were unable to do so despite some effort. 

Is it possible that in control neurons, the cytosolic PV signal localizes within the membrane-bound Kv3.1 signal, with less colocalization, whereas in Kcnc1-A421V/+ neurons, there would be more colocalization of the cytosolic PV and improperly trafficked Kv3.1.? Could the data be presented in this way showing altered colocalization of Kv3.1 with PV?

We do not entirely understand the nature of this concern. In our experiments, we utilized the PV signal to determine the cell membrane and cytosolic compartments in an unbiased manner using a 1-micron shell traced around/outside the edge of the PV signal to define the membrane compartment, with the remainder of the area (minus the nuclear signal defined by DAPI) defined as the cytosol (see Methods 176-186). Because we did not identify any alterations in PV signal or correlation between PV immunohistochemistry and tdTomato expression in Cre reporter strains between WT and Kcnc1-A421V/+ mice, we believe that our strategy for determining membrane:cytosol ratio of Kv3.1 in an unbiased manner is acceptable (albeit of course imperfect). 

Alternatively, membrane fractionation could be performed on WT vs Kcnc1-A421V/+ neurons, followed by Western blotting with a Kv3.1 antibody to show altered proportions in the cytosolic vs. membrane protein fractions. It's important that these results are convincing, as the findings are mentioned in the Abstract, the Results section, and multiple times in the Discussion, although it is still unclear how much the potential altered trafficking contributes to the decrease in K+ currents versus changes in channel gating.

Multiple technical barriers made it difficult for us to gain direct biochemical evidence for altered trafficking of the A421V/+ Kv3.1 variant (see above). It is not clear how membrane fractionation techniques could be easily applied in this case (at least by us) when PV-INs constitute 3-5% of all neocortical neurons. We further agree (as noted above) that it is difficult to properly disentangle the relative roles of impaired membrane trafficking vs. gating deficits to the observed effect; however, we think that both phenomena are likely occurring. In the revised version of the manuscript, we have more explicitly discussed these limitations in the Discussion section (Lines 868-883).   

(2) More information is needed regarding the age of mice used for experiments for the following results (added to the Results section as well as figure legends):

PV density (Supplementary Figure 1) 

K+ current data (Figure 2A-G)       

Kv3.1 localization (Figure 2H and I)        

RTN electrophysiology (Supplementary Figure 3)

Excitatory neuron electrophysiology (Figure 4)             

In vivo 2P calcium imaging (Figure 7) 

Video-EEG (Figure 8)

We apologize for omitting this critical information. In the revised manuscript, we have provided the age of mice for each of our experiments in the results section, in the figure legend, and in the methods section.   

(3) It's unclear why developmental milestones/behavioral assessments were only done at P5-P10. In the previous publication of another Kcnc1 LOF variant (Feng et al. 2024), no differences were found at P5-P10, and it was suggested in the discussion that this finding was "consistent with the known developmental expression pattern of Kv3.1 in mouse, where Kv3.1 protein does not appear until P10 or later". In that paper, they did find behavioral deficits at 2-4 months. Even though this model is more severe than the previous model, it would be interesting to determine if there are any behavioral deficits at a later time point (especially as they find more neurophysiological impairments at P32P42).

As in our previous study, the lack of clear behavioral deficits in developmental milestones from P5-15 is potentially expected considering the developmental expression of Kv3.1, and we performed these experiments primarily to showcase that the Kcnc1-A421V/+ mice exhibit otherwise normal overall early development (although this could be an artifact of the sensitivity of our testing methods).

For the revised manuscript, we have conducted additional experiments to investigate behavioral deficits in adult Kcnc1-A421V/+ mice. We found cognitive/learning deficits in both Kcnc1-A421V/+ mice relative to WT in both the Barnes maze (Figure 2A-C) and Ymaze (Figure 2D-F). Other aspects of animal behavior including cerebellar-related motor function are likely also impaired at post-weaning timepoints, and will be included in a forthcoming research study focusing on the motor function in these mice.  

(4) In the Results section, it should be more clearly stated which cortical layer/layers are being studied. In some cases, it mentions layers 2-4, and in some, only layer 4, and in others, it doesn't mention layers at all. Toward the beginning of the Results section, the rationale for focusing on layers 2-4 to assess the effects of this variant should be well described and then, for each experiment, it should be stated which cortical layers were assessed. Related to this point, it seems electrophysiology was only done in layer 4; the rationale for this should also be included.

We have now clarified which neocortical layers were under investigation in the study. All PV-INs were targeted in somatosensory layers II-IV, while excitatory neurons were either cortical layer IV spiny stellate cells or pyramidal cells. Paired recordings were also completed in layer IV. We have also more explicitly articulated our rationale for looking at PV-INs in layers II-IV to examine the cellular/circuitlevel impact of Kv3.1 in a model of developmental and epileptic encephalopathy (Lines 487-491). 

(5) Kcnc1-A421V/+ PV neurons showed more robust impairments in AP shape and firing at P32-42 than at P16-21 (Figure 3), and only showed synaptic neurotransmission alterations at P32-42 (Figure 6). Thus, it's unclear why Kcnc1-A421V/+ excitatory neurons were only assessed at P16-21 (Figure 4 and Supplementary Figure 4 related to Figure 5), particularly if only secondary or indirect effects on this population would be expected.

We appreciate this excellent point raised by the Reviewer and we have taken the suggestion to examine excitatory neurons at P32-42 in addition to the earlier juvenile timepoint. Our new results from the later timepoint are similar to our results at P16-21: Excitatory neurons show no statistically significant impairments in intrinsic excitability at either of the two timepoints examined (Supplementary Figure 7). This adds support to our original conclusion that PV-INs represent the major driver of disease pathology across development.   

(6) The 2P calcium imaging experiments are potentially interesting, however, a relationship between these results and the electrophysiology results for PV neurons is lacking. Was there an attempt to assess the frequency and/or amplitude of calcium events specifically in PV neurons, outside of the hypersynchronous discharges, to determine whether there are differences between WT and Kcnc1-A421V/+, as was seen in the electrophysiological analyses? It does seem there are some key differences between the two experiments (age: later timepoint for 2P vs. P16-21 and P32-42, layer: 2/3 vs. 4, and PV marking method: virus vs. mouse line), but the electrophysiological differences reported were quite strong. Thus, it would be surprising if there were no alterations in calcium activity among the Kcnc1-A421V/+ PV neurons.

In our initial experiments, the prominent neuropil GCaMP signal in Kcnc1-A421V/+ mice rendered it difficult to distinguish and accurately describe baseline neuronal excitability in PV-INs and non-PV cells. In our revised manuscript, we utilized a soma-tagged GCaMP8m and separately labeled PV-INs through S5E2-tdTomato. This strategy made it possible to assess the amplitude and frequency of calcium transients in both PV-positive and PV-negative cells in vivo. We have updated the description of our methods (lines 230-271) and our results (lines 630-657) in the revised manuscript.

As noted above, our more detailed analysis of somatic calcium transients in PV-IN and non-PV cells during quiet rest (Figure 8 and Supplementary Figure 9) shows that PV-INs from Kcnc1-A421V/+ mice are abnormally excitable- having reduced transient amplitude relative to WT controls. Interestingly, non-PV cells also exhibited an increased calcium transient frequency and reduced amplitude which is potentially consistent with reduced perisomatic inhibition causing disinhibition in cortical microcircuits. We again highlight that the slow kinetics of GCaMP combined with the calcium buffering and brief spikes of PVINs render quantification of action potential frequency and comparisons between groups difficult.  

(7) As mentioned above, it would be helpful to state the time points or age ranges of these experiments to better understand the results and relate them to each other. For example, the 2P imaging showed apparent myoclonic seizures in 7/7 Kcnc1-A421V/+ mice (recorded for a total of 30-50 minutes/mouse), but the video-EEG showed myoclonic seizures in only 3/11 Kcnc1-A421V/+ mice (recorded for 48-72 hours/mouse). Were these experiments done at very different age ranges, so this difference could be due to some sort of progression of seizure types and events as the mice age? Is it possible these are not the same seizure types (even though they are similarly described)? This discrepancy should be discussed.

Mice in the EEG experiments were between the ages of P24 and 48, slightly younger than the age in which we carried out the in vivo calcium imaging experiments (>P50). Therefore, an age-related exacerbation in myoclonic jerks is possible. 

As is highlighted by the Reviewer, it is interesting that the myoclonic seizures were only detected in a portion of the Kcnc1-A421V/+ mice during EEG monitoring (4/12). We believe that the difference is most likely driven by more sensitive detection of the myoclonic jerk activity and behavior in the 2P imaging of neuropil cellular activity compared to our video-EEG monitoring and 2P imaging of soma-tagged GCaMP. We have occasionally observed repetitive myoclonic jerking in mice that appears highly localized (i.e. one forepaw only) suggesting that the myoclonic seizures exist on a spectra of severity from focal to diffuse. It is therefore possible that myoclonic events and electrographic activity may be slightly underestimated in our video-EEG experiments? 

We have now added a few lines discussing this discrepancy in the Discussion (lines 809814).   

(8) Myoclonic jerks and other types of more subtle epileptiform activity have been observed in control mice. Was video-EEG performed on control mice? These data should be added to Figure 8.

We have added recordings in control WT mice (N=4). We did not detect myoclonic jerks or other epileptiform activity in the control mice (Figure 9).  

Minor

(1) In the first Results section, Line 365, the P value (P<0.001) is different from that in the legend for Figure 1, line 743 (P<0.0001).

We have fixed this discrepancy. 

(2) For Supplementary Figure 1, it would be helpful to show images that span the cortical layers (1-6), as PV and Kv3.1 are both expressed across the cortical layers.

We have updated Supplementary Figure 1 with better example images that span the cortical layers.    

(3) Error bars should be added to the line graphs in Supplementary Figure 2, particularly panels B and C. Some of the differences appear small considering the highly significant p-values (i.e. body weight at P7 and brain weight at P21).

The values shown in Supplementary Figure 2D-E are percentages of mice displaying a particular characteristic, so there is no variance for the data.

Supplementary Figure 2B-C actually do contain error bars plotted as SEM, however, because of the large number of N and small degree of variance in the measurements, the error bars are not apparent in the graphs. This has been noted in the Supplementary Figure 2 legend for clarity. 

(4) In Figure 3, although the Kcnc1-A421V/+ neurons have elevated AP amplitudes relative to WT, the representative traces for P16-21 and P32-42 groups appear strikingly opposite (traces in B in G appear to have much higher amplitudes than those in C and H). As this is one of the three AP phenotypes described, it would be nice to have it reflected in the traces.

We have updated our example traces to better represent our main findings including AP amplitude for both P16-21 and P32-42 timepoints.  

(5) Were any effects on the AHP assessed in the electrophysiology experiments? As other studies have reported the effects of altered Kv3 channel activity on AHP, this parameter could be interesting to report as well.

We have now provided data on the afterhyperpolarization for each condition displayed in the Supplementary data tables. Interestingly, we failed to detect significant differences in AHP between WT and Kcnc1-A421V/+ PV-INs, RTN neurons, or pyramidal cells, although we did identify differences in the dV/dt of the repolarization phase of the AP.   

(6) The figure legend for Figure 7 has errors in the panel labeling (D instead of C, and two Fs).

This error has been corrected in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

Specific comments and questions for the authors:         

(1) Do the authors provide a reason for why the juvenile animals are unaffected by the A421V mutation? Is it that PV cells have not fully integrated at this early time point or that Kv3.1 expression is low? Is the developmental expression profile of Kv3.1 in PV cells known and if so could the authors update the discussion with this information?

We interpret the normal early developmental milestones (P5-P15) to reflect that Kcnc1-A421V/+ mice exhibit the onset of their neurological impairment at the same time that PV-INs upregulate Kv3.1, develop a fast-spiking physiological phenotype, and integrate into functional circuits in the third and fourth postnatal weeks. We have updated the discussion (Line 780-782) with this information and more clearly describe our interpretation of these early-life behavioral experiments.   

(2) I would like to see a more complete analysis of the Video-EEG data that is included in Figure 8. What was the seizure duration and frequency? Were there spike-wave seizure types observed? Were EEG events that involve thalamocortical circuitry affected such as spindles? Was sleep architecture impaired in the model? Were littermate control animals recorded?

Although classical convulsive seizures represent only part of the overall epilepsy phenotype that this mouse exhibits, we agree that reporting seizure duration and frequency is important. We have now included this in our revised manuscript (line 624-626). We have also now added WT control mice to our dataset, and, as expected, we failed to observe any epileptic features in our WT recordings.

In our EEG experiments, we did not record EMG activity in the mouse to allow for unambiguous determination of sleep vs. quiet wakefulness. For that reason, and because we believe it beyond the scope of this particular study, we did not examine sleep-related EEG phenomena such as spindles or sleep architecture. We have, however, added a line in the discussion (line 771-774) suggesting that future studies focus on a more thorough investigation of the EEG activity in these animals. 

(3) The in vivo calcium imaging data shows synchronous bursts in A421V animals which is in agreement with the synchronous bursts observed in the EEG. Overall the analysis of the in vivo calcium imaging data appears to be rudimentary and perhaps this is a missed opportunity. What additional insights were gained from this technically demanding experiment that were not obtained from the EEG recordings?

As noted above, in the revised version of the manuscript, we have conducted additional experiments which allowed us to separately examine PV-IN and non-PV neuron excitability via 2P in vivo calcium imaging. This required an alternative strategy to label individual neuronal somata without contamination by the robust neuropil signal that we observed in the approach undertaken in the original submission. We’ve described the details of this new approach in methods (Lines 230-271) and results section (lines 630-657).

Our new results (Figure 8 and Supplementary Figure 9) reveal that, during quiet rest, neocortical PV-INs from Kcnc1-A421V/+ mice exhibit a reduction in calcium transient amplitude during quiet wakefulness and that non-PV cells exhibit altered transient frequency and amplitude. Overall, we believe that these results are consistent with the view that PV-IN-mediated perisomatic inhibition is compromised in Kcnc1-A421V/+ mice which leads to a downstream hyperexcitability in excitatory neurons within cortical microcircuits.  

(4) The increased severity of seizure phenotypes observed in the A421V model relative to knockout mice is interesting but also confusing given what is known about this mutation. As the authors point out, a possible explanation is that the mutation is acting in a dominant negative manner, where mutant Kv3.1 channels compete with other Kvs that would otherwise be able to partially compensate for the loss of Kv function. Alternatively, the A421V mutation might act by affecting the trafficking of heterotetrameric Kv3 channels to the membrane. Can the authors clarify why a trafficking deficit would produce a different effect than a loss of function mutation? Are the authors proposing that a hypomorphic mutation involving both a partial trafficking deficit and a dominant negative effect of those channels that are properly localized is more severe than a "clean" loss of function? The roughly 50% loss of potassium current absent a change in gating would be expected to behave like a loss-of-function mutation. This might be addressed by comparing the surface expression of the other Kv channels and/or through the use of Kv3.1-selective pharmacology.

These are excellent points raised by the Reviewer. As noted above, we have endeavored to clarify our hypothesis as to the basis of this phenomenon, although the mechanistic basis for the more severe phenotype in the Kcnc1-A421V/+ mouse relative to the Kv3.1 knockout is not entirely clear. Our physiology results and the evidence presented supporting a trafficking impairment, are consistent with dominant negative action of the Kv3.1 A421V variant at the level of channel gating and/or trafficking. To restate, we think the Kcnc1-A421V/+ heterozygous variant is more severe than a Kv3.1 knockout for (at least) three reasons: variant Kv3.1 is incorporated into Kv3.1/Kv3.2 heterotetramers to (1) impair trafficking to the membrane as well as (2) alter the electrophysiological function of those channels that do successfully traffic to the membrane (while Kv3.1 knockout affects Kv3.1 only), and (3) the heterozygous variant may escape compensatory upregulation of Kv3.2 and which is known to occur in Kv3.1 knockout mice.

For example, our data suggests and is consistent with the view that heterotetramers of WT Kv3.1 and Kv3.2 potentially come together with the A421V Kv3.1 subunit in the endoplasmic reticulum and then fail to traffic to the membrane due to the presence of one or more A421V subunit(s), as evidenced by increased Kv3.1 staining in the cytosol in the Kcnc1-A421V/+ mouse relative to WT. This is in contrast to what would occur in the Kv3.1knockout mice as there is no subunit produced from the null allele to impair WT Kv3.2 subunits from forming fully functional Kv3.2 homotetramers to then reach the cell surface and function properly. This is one specific possible mechanism for dominant negative activity.

A non-mutually-exclusive mechanism is that inclusion of one or more Kv3.1 A421V subunits into Kv3 heterotetramers impairs gating and prevents potassium flux such that, even if the tetramer does reach the membrane, that entire tetramer fails to contribute to the total potassium current. This is another possible mechanism for dominant negative function of the A421V subunit.

Experimental elucidation of the precise mechanism of the dominant negative activity of the A421V Kcnc1 variant is beyond the scope of this study; yet, our lab is continuing to work on this. It will likely require dose-response experiments in which various ratios of WT and Kv3.1 A421V subunits are co-expressed in heterologous cells and then recorded for an overall effect on potassium current similar to (Clatot et al., 2017).

In the revised manuscript, we have updated our discussion of these mechanistic considerations for KCNC1-related epilepsy syndromes in lines 868-883 in the Discussion. 

References

Cameron JM et al. (2019) Encephalopathies with KCNC1 variants: genotype-phenotypefunctional correlations. Annals of Clinical and Translational Neurology 6:1263– 1272.

Clatot J, Hoshi M, Wan X, Liu H, Jain A, Shinlapawittayatorn K, Marionneau C, Ficker E, Ha T, Deschênes I (2017) Voltage-gated sodium channels assemble and gate as dimers. Nature Communications 8.

Makinson CD, Tanaka BS, Sorokin JM, Wong JC, Christian CA, Goldin AL, Escayg A, Huguenard JR (2017) Regulation of Thalamic and Cortical Network Synchrony by Scn8a. Neuron 93:1165-1179.e6.

Oliver KL et al. (2017) Myoclonus epilepsy and ataxia due to KCNC1 mutation: Analysis of 20 cases and K+ channel properties. Annals of Neurology 81.

Park J et al. (2019) KCNC1-related disorders: new de novo variants expand the phenotypic spectrum. Annals of Clinical and Translational Neurology 6:1319–1326.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

(1) A detailed comparison between this work and the work of Sun et al. on experimental protocols and reagents in the main text will be beneficial for readers to assess critically.

We have added a Key Reagents Table outlining the key reagents used in our study. In terms of experimental protocols, we replicated those described by Sun et al. in most instances and described any differences when present. With this resubmission, we included additional ZnMP accumulation experiments in liquid media (see point 3 below).

(2) The GaPP used by Sun et al. (purchased from Frontier Scientific) is more effective in killing the worm than the one used in this study (purchased from Santa Cruz). Is the different outcome due to the differences in reagents? Moreover, Sun et al. examined the lethality after 3-4 days, while this work examined the lethality after 72 hours. Would the extra 24 hours make any difference in the result?

We now cite product vender differences as a possible reason for the observed difference in worm death, as the reviewer suggests, on page 8 (see text below) and include these differences in the Key Reagents Table. We also now stress the fact that our experiments included different doses of GaPP and the use of eat-2 mutants as an additional control, which we believe adds rigor and demonstrates the potency of GaPP in our experiments. We decided on assessment at 72 hours, as we deemed it a less nebulous time point as compared to 3-4 days. Most of the observed worm death occurred earlier in this interval, so we believe it is unlikely that large group differences would emerge after an additional 24 hours.

“Exposing worms to GaPP, a toxic heme analog, we observed that nematodes deficient in HRG-9 and HRG-10 displayed increased survival compared to WT worms, consistent with prior work,[13] though the between-group difference was markedly smaller in our study. We required higher GaPP concentrations to induce lethality, potentially due to product vendor differences, but did observe a clear dose-dependent effect across strains. Although it was previously proposed that the survival benefit seen in worms lacking HRG-9 and HRG-10 resulted from reduced transfer from intestinal cells after GaPP ingestion, our data suggest the reduced lethality is more likely due to decreased environmental GaPP uptake. Supporting this notion, DKO worms exhibited lawn avoidance, reduced pharyngeal pumping, and modestly lower intestinal ZnMP accumulation when exposed to this fluorescent heme analog on agar plates. In liquid media, DKO worms demonstrated higher fluorescence, but only in ZnMP-free conditions, suggesting the presence of gut granule autofluorescence. Furthermore, survival following exposure to GaPP was highest in eat-2 mutants, despite heme trafficking being unaffected in this strain.”

(3) This work reported the opposite result of Sun et al. for the fluorescent ZnMP accumulation assay. However, the experimental protocols used by the two studies are massively different. Sun et al. did the ZnMP staining by incubating the L4-stage worms in an axenic mCeHR2 medium containing 40 μM ZnMP (purchased from Frontier Scientific) and 4 μM heme at 20 ℃ for 16 h, while this work placed the L4-stage worms on the OP50 E. coli seeded NGM plates treated with 40 μM ZnMP (purchased from Santa Cruz) for 16 h. The liquid axenic mCeHR2 medium is bacteria-free, heme-free, and consistent for ZnMP uptake by worms. This work has mentioned that the hrg-9 hrg-10 double null mutant has bacterial lawn avoidance and reduced pharyngeal pumping phenotypes. Therefore, the ZnMP staining protocol used in this work faces challenges in the environmental control for the wild type vs. the mutant. The authors should adopt the ZnMP staining protocol used by Sun et al. for a proper evaluation of fluorescent ZnMP accumulation.

We agree with this comment. As such, we performed the ZnMP assay in liquid media conditions, as now described on page 13:

“For liquid media experiments, three generations of worms were cultured in regular heme (20 uM) axenic media, with the first two generations receiving antibiotic-supplemented media (10 mg/ml tetracycline) and the 3^rd generation cultivated without antibiotic. L4 worms from the 3^rd generation were placed in media containing 40uM ZnMP for 16 hours before being prepared and mounted for imaging as above. Worms were imaged on Zeiss Axio Imager 2 at 40x magnification, with image settings kept uniform across all images. Fluorescent intensity was measured within the proximal region of the intestine using ImageJ.”

In heme-free media, both WT and DKO worms invariably entered L1 arrest, thus we were not able to replicate the results reported by Sun et al. Using media containing heme, we did see an increase in fluorescence, but this was only in the ZnMP-free condition, indicating that the increased signal was attributable to autofluorescence. This is a known phenomenon associated with gut granules in C. elegans in the setting of oxidative stress. The results of these experiments are now summarized on page 6:

“DKO nematodes at the L4 larval stage were previously shown to accumulate the fluorescent heme analog zinc mesoporphyrin IX (ZnMP) in intestinal cells in low-heme (4 µM) liquid media. While attempting to replicate this experiment, we observed that both wildtype and DKO nematodes entered L1 arrest under these conditions. Therefore, to allow for developmental progression, we grew worms on standard OP50 E. coli plates and in media containing physiological levels of heme (20 µM). We then examined whether differences in ZnMP uptake persisted under these basal conditions. DKO worms grown on ZnMP-treated E. coli plates displayed significantly reduced intestinal ZnMP fluorescence compared to N2 (Figure 1B and C). Using basal heme media with ZnMP, there was no significant difference in ZnMP fluorescence between DKO and wildtype nematodes, although DKO worms grown in media without ZnMP exhibited significantly higher autofluorescence (Figure 1D and E). To test whether autofluorescence may have contributed to the higher fluorescent intensities previously reported in heme-deficient DKO worms, we repeated this experiment on agar plates under starved conditions but did not observe a difference between groups (Figure 1B).”

(4) A striking difference between the two studies is that Sun et al. emphasize the biochemical function of TANGO2 homologs in heme transporting with evidence from some biochemical tests. In contrast, this work emphasizes the physiological function of TANGO2 homologs with evidence from multiple phenotypical observations. In the discussion part, the authors should address whether these observed phenotypes in this study can be due to the loss of heme transporting activities upon eliminating TANGO2 homologs. This action can improve the merit of academic debate and collaboration.

Thank you for this suggestion. The following text has been added to the Discussion section (page 9):

“In addition to altered pharyngeal pumping, DKO worms displayed multiple previously unreported phenotypic features, suggesting a broader metabolic impairment and reminiscent of some clinical manifestations observed in patients with TDD. Elucidating the mechanisms underlying this phenotype, and whether they reflect a core bioenergetic defect, is an active area of investigation in our lab. Several C. elegans heme-responsive genes have been characterized, revealing relatively specific defects in heme uptake or utilization rather than broad organismal dysfunction. For example, hrg-1 and hrg-4 mutants exhibit impaired growth only under heme-limited conditions,[23] and hrg-3 loss affects brood size and embryonic viability specifically when maternal heme is scarce.[24] ]By contrast, hrg-9 and hrg-10 mutants exhibit the most severe organismal phenotypes of the hrg family, to date, including reduced pharyngeal pumping, decreased motility, shortened lifespan, and smaller broods, even when fed a heme-replete diet.”

Reviewer #2 (Public review):

(1) The manuscript is written mainly as a criticism of a previously published paper. Although reproducibility in science is an issue that needs to be acknowledged, a manuscript should focus on the new data and the experiments that can better prove and strengthen the new claims.

Thank you for this suggestion. While the primary intent of this study was to replicate key findings from the 2022 publication by Sun et al., the revised manuscript now emphasizes underlying mechanisms more broadly rather than focusing narrowly on that prior publication.

(2) The current presentation of the logic of the study and its results does not help the authors deliver their message, although they possess great potential.

We have attempted to rectify this through substantial revision of the Discussion section and other places throughout the manuscript.

(3) The study is missing experiments to link hrg-9 and hrg-10 more directly to bioenergetic and oxidative stress pathways.

The reviewer is correct in this assertion, but it was not our intent to definitively prove this link or, indeed, the primary mechanism of TANGO2 in the present manuscript. This said, we are actively engaged in this endeavor in our lab and anticipate these data will be published in a separate, forthcoming publication.

We have added additional references pertaining to hrg-9 enrichment as part of the mitochondrial unfolded protein response (page 10) and a comparison of the phenotype observed in hrg-9 and hrg-10 deficient worms versus those lacking other proteins in the hrg family (page 9).

Reviewer #3 (Public review):

(1) The authors stress - with evidence provided in this paper or indicated in the literature - that the primary role of TANGO2 and its homologues is unlikely to be related to heme trafficking, arguing that observed effects on heme transport are instead downstream consequences of aberrant cellular metabolism. But in light of a mounting body of evidence (referenced by the authors) connecting more or less directly TANGO2 to heme trafficking and mobilization, it is recommended that the authors comment on how they think TANGO2 could relate to and be essential for heme trafficking, albeit in a secondary, moonlighting capacity. This would highlight a seemingly common theme in emerging key players in intracellular heme trafficking, as it appears to be the case for GAPDH - with accumulating evidence of this glycolytic enzyme being critical for heme delivery to several downstream proteins.

TANGO2 is essential for mitochondrial health, albeit in a yet unknown capacity. In the absence of TANGO2, defects in heme trafficking may be secondary sequelae of mitochondrial dysfunction. We would point out that prior studies that attempted to show that TANGO2 and its homologs are involved in heme trafficking proposed very different mechanisms (direct binding vs. membrane protein interaction) and relied on artificially low or high heme conditions to produce these effects. We have attempted to address these more clearly in the Discussion section and have added a fifth figure to summarize our current unifying theory for how heme levels and mitochondrial stress may be linked.

(2) The observation - using eat-2 mutants and lawn avoidance behaviour - that survival patterns can be partially explained by reduced consumption, is fascinating. It would be interesting to quantify the two relative contributions.

We have completed additional ZnMP experiments in liquid media at the reviewers’ request. This experimental condition eliminates lawn avoidance as a factor in consumption. Fluorescent intensity was significantly higher in the DKO worms in media lacking ZnMP, indicating increased autofluorescence in DKO worms, while signal was not significantly different in media with ZnMP.

(3) In the legend to Figure 1A it's a bit unclear what the differently coloured dots represent for each condition. Repeated measurements, worms, independent experiments? The authors should clarify this.

The following sentence has been added to the legend for Figure 1:

“Each dot represents the number of offspring laid by one adult worm on one GaPP-treated plate after 24 hours.”

(4) It would help if the entire fluorescence images (raw and processed) for the ZnMP treatments were provided. Fluorescence images would also benefit Figure 1B.

Fluorescent intensity values pertaining to the ZnMP experiments are included in our Extended Data supplement, and we have added representative images to Figure 1, per the reviewer’s request. We thank the reviewer for this helpful suggestion. We would be happy to upload raw images to an open-access repository if deemed necessary by the editorial team.

(5) Increasingly, the understanding of heme-dependent roles relies on transient or indirect binding to unsuspected partners, not necessarily relying on a tight affinity and outdating the notion of heme as a static cofactor. Despite impressive recent advancements in the detection of these interactions (for example https://doi.org/10.1021/jacs.2c06104; cited by the authors), a full characterisation of the hemome is still elusive. Sandkuhler et al. deemed it possible but seem to question that heme binding to TANGO2 occurs. However, Sun et al. convincingly showed and characterised TANGO2 binding to heme. It is recommended that the authors comment on this.

We believe it is plausible that TANGO2 binds heme (as do hundreds of other proteins), especially as it has been shown to bind other hydrophobic molecules. However, we also note that a separate paper examining the role of TANGO2 in heme transport posited that GAPDH is the sole heme binding partner for cytoplasmic transport (https://doi.org/10.1038/s41467-025-62819-2), contradicting the originally posited theory of how TANGO2 functions. This is described in the Discussion section and, as noted above, we have added an additional figure to demonstrate our unifying hypothesis for why TANGO2 may be important in the low-heme state, irrespective of any direct effect on heme trafficking.

Additional comments and revisions:

(1) It was suggested that a triple mutant (eat-2; hrg-9; hrg-10) be tested to determine the primary driver of GaPP toxicity. We appreciate this suggestion, but we offer the following rationale for why these experiments were not pursued. The eat-2 mutant, which lacks a nicotinic acetylcholine receptor subunit in pharyngeal muscles, was included solely as a dietary restriction control to illustrate that reduced GaPP toxicity in the hrg-9/10 double mutant could arise from poor feeding rather than defective heme transport. Both eat-2 and hrg-9/10 mutants exhibit markedly reduced feeding but via different mechanisms. In our assays, GaPP survival was inversely correlated with ingestion rate: eat-2 animals, which feed the least, showed the highest survival, while hrg-9/10 mutants showed intermediate feeding and intermediate survival. Consistent with this, eat-2 worms also displayed the lowest ZnMP accumulation.

(2) GaPP solution was added to NGM plates after seeding with OP50. This is now expressly stated in the Methods section (page 15). We would note that Sun et al. mixed GaPP in with NGM in the liquid phase. We would expect that if there were a difference in GaPP exposure due to these different protocols, worms in our experiment would have received higher GaPP concentrations.

“Standard NGM plates were treated with 1, 2, 5, or 10 µM gallium protoporphyrin IX (GaPP; Santa Cruz) after seeding with OP50. Plates were swirled to ensure an even distribution of GaPP and allowed to dry completely.

(3) The manuscript has been reworked to read as more of an independent study rather than a rebuttal of prior work, though the primary objective of validating prior work remains unchanged.

(4) Several technical details of experiments have been moved from the main text to the materials and methods section.

(5) One reviewer noted that the figure numbering should be adjusted. Numbering does not progress sequentially (i.e., 1A…1B…2A…2B) early in the text, because we have opted to consolidate data pertaining to heme analog experiments in Figure 1 and behavioral data in Figure 2.

(6) “Kingdoms” has been changed to “domains” (page 4).

(7) Example images are now included for Figure 1B, as noted above.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment:

This study introduces an important approach using selection linked integration (SLI) to generate Plasmodium falciparum lines expressing single, specific surface adhesins PfEMP1 variants, enabling precise study of PfEMP1 trafficking, receptor binding, and cytoadhesion. By moving the system to different parasite strains and introducing an advanced SLI2 system for additional genomic edits, this work provides compelling evidence for an innovative and rigorous platform to explore PfEMP1 biology and identify novel proteins essential for malaria pathogenesis including immune evasion.

Reviewer #1 (Public review):

One of the roadblocks in PfEMP1 research has been the challenges in manipulating var genes to incorporate markers to allow the transport of this protein to be tracked and to investigate the interactions taking place within the infected erythrocyte. In addition, the ability of Plasmodium falciparum to switch to different PfEMP1 variants during in vitro culture has complicated studies due to parasite populations drifting from the original (manipulated) var gene expression. Cronshagen et al have provided a useful system with which they demonstrate the ability to integrate a selectable drug marker into several different var genes that allows the PfEMP1 variant expression to be 'fixed'. This on its own represents a useful addition to the molecular toolbox and the range of var genes that have been modified suggests that the system will have broad application. As well as incorporating a selectable marker, the authors have also used selective linked integration (SLI) to introduce markers to track the transport of PfEMP1, investigate the route of transport, and probe interactions with PfEMP1 proteins in the infected host cell.

What I particularly like about this paper is that the authors have not only put together what appears to be a largely robust system for further functional studies, but they have used it to produce a range of interesting findings including:

Co-activation of rif and var genes when in a head-to-head orientation.

The reduced control of expression of var genes in the 3D7-MEED parasite line.

More support for the PTEX transport route for PfEMP1.

Identification of new proteins involved in PfEMP1 interactions in the infected erythrocyte, including some required for cytoadherence.

In most cases the experimental evidence is straightforward, and the data support the conclusions strongly. The authors have been very careful in the depth of their investigation, and where unexpected results have been obtained, they have looked carefully at why these have occurred.

We thank the reviewer for the kind assessment and the comments to improve the paper.

(1) In terms of incorporating a drug marker to drive mono-variant expression, the authors show that they can manipulate a range of var genes in two parasite lines (3D7 and IT4), producing around 90% expression of the targeted PfEMP1. Removal of drug selection produces the expected 'drift' in variant types being expressed. The exceptions to this are the 3D7-MEED line, which looks to be an interesting starting point to understand why this variant appears to have impaired mutually exclusive var gene expression and the EPCR-binding IT4var19 line. This latter finding was unexpected and the modified construct required several rounds of panning to produce parasites expressing the targeted PfEMP1 and bind to EPCR. The authors identified a PTP3 deficiency as the cause of the lack of PfEMP1 expression, which is an interesting finding in itself but potentially worrying for future studies. What was not clear was whether the selected IT4var19 line retained specific PfEMP1 expression once receptor panning was removed.

We do not have systematic long-term data for the Var19 line but do have medium-term data. After panning the Var19 line, the binding assays were done within 3 months without additional panning. The first binding assay was 2 months after the panning and the last binding assays three weeks later, totaling about 3 months without panning. While there is inherent variation in these assays that precludes detection of smaller changes, the last assay showed the highest level of binding, giving no indication for rapid loss of the binding phenotype. Hence, we can say that the binding phenotype appears to be stable for many weeks without panning the cells again and there was no indication for a rapid loss of binding in these parasites.

Systematic long-term experiments to assess how long the Var19 parasites retain binding would be interesting, but given that the binding-phenotype appears to remain stable over many weeks or even months, this would only make sense if done over a much longer time frame. Such data might arise if the line is used over extended times for a specific project in which case it might be advisable to monitor continued binding. We included a statement in the discussion that the binding phenotype was stable over many weeks but that if long-term work with this line is planned, monitoring the binding phenotype might be advisable: “In the course of this work the binding phenotype of the IT4var19 expressor line remained stable over many weeks without further panning. However, given that initial panning had been needed for this particular line, it might be advisable for future studies to monitor the binding phenotype if the line is used for experiments requiring extended periods of cultivation.”

(2) The transport studies using the mDHFR constructs were quite complicated to understand but were explained very clearly in the text with good logical reasoning.

We are aware of this being a complex issue and are glad this was nevertheless understandable.

(3) By introducing a second SLI system, the authors have been able to alter other genes thought to be involved in PfEMP1 biology, particularly transport. An example of this is the inactivation of PTP1, which causes a loss of binding to CD36 and ICAM-1. It would have been helpful to have more insight into the interpretation of the IFAs as the anti-SBP1 staining in Figure 5D (PTP-TGD) looks similar to that shown in Figure 1C, which has PTP intact. The anti-EXP2 results are clearly different.

We realize the description of the PTP1-TGD IFA data and that of the other TGDs (see also response to Recommendation to authors point 4 and reviewer 2, major points 6 and 7) was rather cursory. The previously reported PTP1 phenotype is a fragmentation of the Maurer’s clefts into what in IFA appear to be many smaller pieces (Rug et al 2014, referenced in the manuscript). The control in Fig. 5D has 13 Maurer’s cleft spots (previous work indicates an average of ~15 MC per parasite, see e.g. the originally co-submitted eLife preprint doi.org/10.7554/eLife.103633.1 and references therein). The control mentioned by the reviewer in Fig. 1C has about 22 Maurer’s clefts foci, at the upper end of the typical range, but not unusual. In contrast, the PTP1-TGD in Fig. 5D, has more than 30 foci with an additional cytoplasmic pool and additional smaller, difficult to count foci. This is consistent with the published phenotype in Rug et al 2014. The EXP1 stained cell has more than 40 Maurer’s cleft foci, again beyond what typically is observed in controls. Therefore, these cells show a difference to the control in Fig. 5 but also to Fig. 1C. Please note that we are looking at two different strains, in Fig. 1 it is 3D7 and in Fig. 5 IT4. While we did not systematically assess this, the Maurer’s clefts number per cell seemed to be largely comparable between these strains (Fig. 10C and D in the other eLife preprint doi.org/10.7554/eLife.103633.1). 

Overall, as the PTP1 loss phenotype has already been reported, we did not go into more experimental detail. However, we now modified the text to more clearly describe how the phenotype in the PTP1-TGD parasites was different to control: “IFAs showed that in the PTP1-TGD parasites, SBP1 and PfEMP1 were found in many small foci in the host cell that exceeded the average number of ~ 15 Maurer’s clefts typically found per infected RBC [66] (Fig. 5D). This phenotype resembled the previously reported Maurer’s clefts phenotype of the PTP1 knock out in CS2 parasites [39].”

(4) It is good to see the validation of PfEMP1 expression includes binding to several relevant receptors. The data presented use CHO-GFP as a negative control, which is relevant, but it would have been good to also see the use of receptor mAbs to indicate specific adhesion patterns. The CHO system if fine for expression validation studies, but due to the high levels of receptor expression on these cells, moving to the use of microvascular endothelial cells would be advisable. This may explain the unexpected ICAM-1 binding seen with the panned IT4var19 line.

We agree with the reviewer that it is desirable to have better binding systems for studying individual binding interactions. As the main purpose of this paper was to introduce the system and provide proof of principle that the cells show binding, we did not move to more complicated binding systems. However, we would like to point out that the CSA binding was done on receptor alone in addition to the CSA-expressing HBEC-5i cells and was competed successfully with soluble CSA. In addition, apart from the additional ICAM1-binding of the Var19 line, all binding phenotypes were conform with expectations. We therefore hope the tools used for binding studies are acceptable at this stage of introducing the system while future work interested in specific PfEMP1 receptor interactions may use better systems, tailored to the specific question (e.g. endothelial organoid models and engineered human capillaries and inhibitory antibodies or relevant recombinant domains for competition).

(5) The proxiome work is very interesting and has identified new leads for proteins interacting with PfEMP1, as well as suggesting that KAHRP is not one of these. The reduced expression seen with BirA* in position 3 is a little concerning but there appears to be sufficient expression to allow interactions to be identified with this construct. The quantitative impact of reduced expression for proxiome experiments will clearly require further work to define it.

This is a valid point. Clearly there seems to be some impact on binding when BirA* is placed in the extracellular domain (either through reduced presentation or direct reduction of binding efficiency of the modified PfEMP1; please see also minor comment 10 reviewer 2). The exact quantitative impact on the proxiome is difficult to assess but we note that the relative enrichment of hits to each other is rather similar to the other two positions (Fig. 6H-J). We therefore believe the BioIDs with the 3 PfEMP1-BirA* constructs are sufficient to provide a general coverage of proteins proximal to PfEMP1 and hope this will aid in the identification of further proteins involved in PfEMP1 transport and surface display as illustrated with two of the hits targeted here.

The impact of placing a domain on the extracellular region of PfEMP1 will have to be further evaluated if needed in other studies. But the finding that a large folded domain can be placed into this part at all, even if binding was reduced, in our opinion is a success (it was not foreseeable whether any such change would be tolerated at all).

(6) The reduced receptor binding results from the TryThrA and EMPIC3 knockouts were very interesting, particularly as both still display PfEMP1 on the surface of the infected erythrocyte. While care needs to be taken in cross-referencing adhesion work in P. berghei and whether the machinery truly is functionally orthologous, it is a fair point to make in the discussion. The suggestion that interacting proteins may influence the "correct presentation of PfEMP1" is intriguing and I look forward to further work on this.

We hope future work will be able to shed light on this.

Overall, the authors have produced a useful and reasonably robust system to support functional studies on PfEMP1, which may provide a platform for future studies manipulating the domain content in the exon 1 portion of var genes. They have used this system to produce a range of interesting findings and to support its use by the research community. Finally, a small concern. Being able to select specific var gene switches using drug markers could provide some useful starting points to understand how switching happens in P. falciparum. However, our trypanosome colleagues might remind us that forcing switches may show us some mechanisms but perhaps not all.

Point noted! From non-systematic data with the Var01 line that has been cultured for extended periods of time (several years), it seems other non-targeted vars remain silent in our SLI “activation” lines but how much SLI-based var-expression “fixing” tampers with the integrity of natural switching mechanisms is indeed very difficult to gage at this stage. We now added a statement to the discussion that even if mutually exclusive expression is maintained, it is not certain the mechanisms controlling var expression all remain intact: “However, it should be noted that it is not known whether all mechanisms controlling mutually exclusive expression and switching remain intact in parasites with SLI-activated var genes.”

Reviewer #2 (Public review):

Summary

Croshagen et al develop a range of tools based on selection-linked integration (SLI) to study PfEMP1 function in P. falciparum. PfEMP1 is encoded by a family of ~60 var genes subject to mutually exclusive expression. Switching expression between different family members can modify the binding properties of the infected erythrocyte while avoiding the adaptive immune response. Although critical to parasite survival and Malaria disease pathology, PfEMP1 proteins are difficult to study owing to their large size and variable expression between parasites within the same population. The SLI approach previously developed by this group for genetic modification of P. falciparum is employed here to selectively and stably activate the expression of target var genes at the population level. Using this strategy, the binding properties of specific PfEMP1 variants were measured for several distinct var genes with a novel semi-automated pipeline to increase throughput and reduce bias. Activation of similar var genes in both the common lab strain 3D7 and the cytoadhesion competent FCR3/IT4 strain revealed higher binding for several PfEMP1 IT4 variants with distinct receptors, indicating this strain provides a superior background for studying PfEMP1 binding. SLI also enables modifications to target var gene products to study PfEMP1 trafficking and identify interacting partners by proximity-labeling proteomics, revealing two novel exported proteins required for cytoadherence. Overall, the data demonstrate a range of SLI-based approaches for studying PfEMP1 that will be broadly useful for understanding the basis for cytoadhesion and parasite virulence.

We thank the reviewer for the kind assessment and the comments to improve the paper.

Comments

(1) While the capability of SLI to actively select var gene expression was initially reported by Omelianczyk et al., the present study greatly expands the utility of this approach. Several distinct var genes are activated in two different P. falciparum strains and shown to modify the binding properties of infected RBCs to distinct endothelial receptors; development of SLI2 enables multiple SLI modifications in the same parasite line; SLI is used to modify target var genes to study PfEMP1 trafficking and determine PfEMP1 interactomes with BioID. Curiously, Omelianczyk et al activated a single var (Pf3D7_0421300) and observed elevated expression of an adjacent var arranged in a head-to-tail manner, possibly resulting from local chromatin modifications enabling expression of the neighboring gene. In contrast, the present study observed activation of neighboring genes with head-to-head but not head-totail arrangement, which may be the result of shared promoter regions. The reason for these differing results is unclear although it should be noted that the two studies examined different var loci.

The point that we are looking at different loci is very valid and we realize this is not mentioned in the discussion. We now added to the discussion that it is unclear if our results and those cited may be generalized and that different var gene loci may respond differently

“However, it is unclear if this can be generalized and it is possible that different var loci respond differently.”

(2) The IT4var19 panned line that became binding-competent showed increased expression of both paralogs of ptp3 (as well as a phista and gbp), suggesting that overexpression of PTP3 may improve PfEMP1 display and binding. Interestingly, IT4 appears to be the only known P. falciparum strain (only available in PlasmoDB) that encodes more than one ptp3 gene (PfIT_140083100 and PfIT_140084700). PfIT_140084700 is almost identical to the 3D7 PTP3 (except for a ~120 residue insertion in 3D7 beginning at residue 400). In contrast, while the C-terminal region of PfIT_140083100 shows near-perfect conservation with 3D7 PTP3 beginning at residue 450, the N-terminal regions between the PEXEL and residue 450 are quite different. This may indicate the generally stronger receptor binding observed in IT4 relative to 3D7 results from increased PTP3 activity due to multiple isoforms or that specialized trafficking machinery exists for some PfEMP1 proteins.

We thank the reviewer for pointing this out, the exact differences between the two PTP3s of IT4 and that of other strains definitely should be closely examined if the function of these proteins in PfEMP1 binding is analysed in more detail. 

It is an interesting idea that the PTP3 duplication could be a reason for the superior binding of IT4. We always assumed that IT4 had better binding because it was less culture adapted but this does not preclude that PTP3(s) is(are) a reason for this. However, at least in our 3D7 PTP3 can’t be the reason for the poor binding, as our 3D7 still has PfEMP1 on the surface while in the unpanned IT4-Var19 line and in the Maier et al., Cell 2008 ptp3 KO (PMID: 18614010)) PfEMP1 is not on the surface anymore. 

Testing the impact of having two PTP3s would be interesting, but given the “mosaic” similarity of the two PTP3s isoforms, a simple add-on experiment might not be informative. Nevertheless, it will be interesting in future work to explore this in more detail.

Reviewer #3 (Public review):

Summary:

The submission from Cronshagen and colleagues describes the application of a previously described method (selection linked integration) to the systematic study of PfEMP1 trafficking in the human malaria parasite Plasmodium falciparum. PfEMP1 is the primary virulence factor and surface antigen of infected red blood cells and is therefore a major focus of research into malaria pathogenesis. Since the discovery of the var gene family that encodes PfEMP1 in the late 1990s, there have been multiple hypotheses for how the protein is trafficked to the infected cell surface, crossing multiple membranes along the way. One difficulty in studying this process is the large size of the var gene family and the propensity of the parasites to switch which var gene is expressed, thus preventing straightforward gene modification-based strategies for tagging the expressed PfEMP1. Here the authors solve this problem by forcing the expression of a targeted var gene by fusing the PfEMP1 coding region with a drug-selectable marker separated by a skip peptide. This enabled them to generate relatively homogenous populations of parasites all expressing tagged (or otherwise modified) forms of PfEMP1 suitable for study. They then applied this method to study various aspects of PfEMP1 trafficking.

Strengths:

The study is very thorough, and the data are well presented. The authors used SLI to target multiple var genes, thus demonstrating the robustness of their strategy. They then perform experiments to investigate possible trafficking through PTEX, they knock out proteins thought to be involved in PfEMP1 trafficking and observe defects in cytoadherence, and they perform proximity labeling to further identify proteins potentially involved in PfEMP1 export. These are independent and complimentary approaches that together tell a very compelling story.

We thank the reviewer for the kind assessment and the comments to improve the paper.

Weaknesses:

(1)  When the authors targeted IT4var19, they were successful in transcriptionally activating the gene, however, they did not initially obtain cytoadherent parasites. To observe binding to ICAM-1 and EPCR, they had to perform selection using panning. This is an interesting observation and potentially provides insights into PfEMP1 surface display, folding, etc. However, it also raises questions about other instances in which cytoadherence was not observed. Would panning of these other lines have been successfully selected for cytoadherent infected cells? Did the authors attempt panning of their 3D7 lines? Given that these parasites do export PfEMP1 to the infected cell surface (Figure 1D), it is possible that panning would similarly rescue binding. Likewise, the authors knocked out PTP1, TryThrA, and EMPIC3 and detected a loss of cytoadhesion, but they did not attempt panning to see if this could rescue binding. To ensure that the lack of cytoadhesion in these cases is not serendipitous (as it was when they activated IT4var19), they should demonstrate that panning cannot rescue binding.

These are very important considerations. Indeed, we had repeatedly attempted to pan 3D7 when we failed to get the SLI-generated 3D7 PfEMP1 expressor lines to bind, but this had not been successful. The lack of binding had been a major obstacle that had held up the project and was only solved when we moved to IT4 which readily bound (apart from Var19 which was created later in the project). After that we made no further efforts to understand why 3D7 does not bind but the fact that PfEMP1 is on the surface indicates this is not a PTP3 issue because loss of PTP3 also leads to loss of PfEMP1 surface display. Also, as the parent 3D7 could not be panned, we assumed this issue is not easily fixed in the SLI var lines we made in 3D7.

Panning the TGD lines: we see the reasoning for conducting panning experiments with the TGD lines. However, on second thought, we are unsure this should be attempted. The outcome might not be easily interpretable as at least two forces will contribute to the selection in panning experiments with TGD lines that do not bind anymore:

Firstly, panning would work against the SLI of the TGD, resulting in a tug of war between the TGD-SLI and binding. This is because a small number of parasites will loop out the TGD plasmid (revert) and would normally be eliminated during standard culturing due to the SLI drug used for the TGD. These revertant cells would bind and the panning would enrich them. Hence, panning and SLI are opposed forces in the case of a TGD abolishing binding. It is unclear how strong this effect would be, but this would for sure lead to mixed populations that complicate interpretations. 

The second selecting force are possible compensatory changes to restore binding. These can be due to different causes: (i) reversal of potential independent changes that may have occurred in the TGD parasites and that are in reality causing the binding loss (i.e. such as ptp3 loss or similar, the concern of the reviewer) or (ii) new changes to compensate the loss of the TGD target (in this case the TGD is the cause of the binding loss but for instance a different change ameliorates it by for instance increasing PfEMP1 expression or surface display). As both TGDs show some residual binding and have VAR01 on the surface to at least some extent, it is possible that new compensatory changes might indeed occur that indirectly increase binding again. 

In summary, even if more binding occurs after panning of the lines, it is not clear whether this is due to a compensatory change ameliorating the TGD or reversal of an unrelated change or are counter-selections against the SLI. To determine the cause, the panned TGD lines would need to be subjected to a complex and time-consuming analysis (WGS, RNASeq, possibly Maurer’s clefts phenotype) to find out whether they were SLI-revertants, or had an unrelated chance that was reverted or a new compensatory change that helps binding. This might be further muddled if a mix of cells come out of the selection that have different changes of the options indicated above. In that case, it might even require scRNASeq to make sense of the panning experiment. Due to the envisaged difficulty in interpreting the outcome, we did not attempt this panning.

To exclude loss of ptp3 expression as the reason for binding loss (something we would not have seen in the WGS if it is only due to a transcriptional change), we now carried out RNASeq with the TGD lines that have a binding phenotype. While we did not generate replicas to obtain quantitative data, the results show that both ptp3 copies were expressed in these TGDs comparable to other parasite lines that do bind with the same SLI-activated var gene, indicating that the effect is not due to ptp3 (see response to point 4 on PTP3 expression in the Recommendations for the authors). While we can’t fully exclude other changes in the TGDs that might affect binding, the WGS did not show any obvious alterations that could be responsible for this. 

(2) The authors perform a series of trafficking experiments to help discern whether PfEMP1 is trafficked through PTEX. While the results were not entirely definitive, they make a strong case for PTEX in PfEMP1 export. The authors then used BioID to obtain a proxiome for PfEMP1 and identified proteins they suggest are involved in PfEMP1 trafficking. However, it seemed that components of PTEX were missing from the list of interacting proteins. Is this surprising and does this observation shed any additional light on the possibility of PfEMP1 trafficking through PTEX? This warrants a comment or discussion.

This is an interesting point and we agree that this warrants to be discussed. A likely reason why PTEX components are not picked up as interactors is that BirA* is expected to be unfolded when it passes through the channel and in that state can’t biotinylate. Labelling likely would only be possible if PfEMP1 lingered at the PTEX translocation step before BirA* became unfolded to go through the channel which we would not expect under physiological conditions. We added the following sentences to the discussion: “While our data indicates PfEMP1 uses PTEX to reach the host cell, this could be expected to have resulted in the identification of PTEX components in the PfEMP1 proxiomes, which was not the case. However, as BirA* must be unfolded to pass through PTEX, it likely is unable to biotinylate translocon components unless PfEMP1 is stalled during translocation. For this reason, a lack of PTEX components in the PfEMP1 proxiomes does not necessarily exclude passage through PTEX.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Most of my comments are in the public section. I would just highlight a few things:

(1) In the binding studies section you talk about "human brain endothelial cells (HBEC-5i)". These cells do indeed express CSA but this is a property of their immortalisation rather than being brain endotheliium, which does not express CSA. I think this could be confusing to readers so I think you might want to reword this sentence to focus on CSA expressing the cell line rather than other features.

We thank the reviewer for pointing this out, we now modified the sentence to focus on the fact these are CSA expressing cells and provided a reference for it.

(2) As I said in the public section, CHO cells are great for proof of concept studies, but they are not endothelium. Not a problem for this paper.

Noted! Please also see our response to the public review.

(3) I wonder whether your comment about how well tolerated the Bir3* insertion is may be a bit too strong. I might say "Nonetheless, overall the BirA* modified PfEMP1 were functional."

Changed as requested.

(4) I'm not sure how you explain the IFA staining patterns to the uninitiated, but perhaps you could explain some of the key features you are looking for.

We apologise for not giving an explanation of the IFA staining patterns in the first place. Please see detailed response to public review of this reviewer (point 3 on PTP1-TGD phenotype) and to reviewer 2 (Recommendations to the authors, points 6 and 7 on better explaining and quantifying the Maurer’s clefts phenotypes). For this we now also generated parasites that episomally express mCherry tagged SBP1 in the TGD parasites with the reduced binding phenotype. This resulted in amendments to Fig. S7, addition of a Fig. S8 and updated results to better explain the phenotypes. 

This is a great paper - I just wish I'd had this system before.

Thank you!

Reviewer #2 (Recommendations for the authors):

Major Comments

(1) Does the RNAseq analysis of 3D7var0425800 and 3D7MEEDvar0425800 (Figure 1G, H) reveal any differential gene expression that might suggest a basis for loss of mutually exclusive var expression in the MEED line?

We now carried out a thorough analysis of these RNASeq experiments to look for an underlying cause for the phenotype. This was added as new Figure 1J and new Table S3. This analysis again illustrated the increased transcript levels of var genes. In addition, it showed that transcripts of a number of other exported proteins, including members of other gene families, were up in the MEED line. 

One hit that might be causal of the phenotype was sip2, which was down by close to 8-fold (pAdj 0.025). While recent work in P. berghei found this ApiAP2 to be involved in the expression of merozoite genes (Nishi et al., Sci Advances 2025(PMID: 40117352)), previous work in P. falciparum showed that it binds heterochromatic telomere regions and certain var upstream regions (Flück et al., PlosPath 2010 (PMID: 20195509), now cited in the manuscript). The other notable change was an upregulation of the non-coding RNA ruf6 which had been linked with impaired mono-allelic var expression (Guizetti et al., NAR 2016 (PMID: 27466391), now also cited in the manuscript). While it would go beyond this manuscript to follow this up, it is conceivable that alterations in chromosome end biology due to sip2 downregulation or upregulation of ruf6 are causes of the observed phenotype

We now added a paragraph on the more comprehensive analysis of the RNA Seq data of the MEED vs non-MEED lines at the end of the second results section.

(2) Could the inability of the PfEMP1-mDHFR fusion to block translocation (Fig 2A) reflect unique features of PfEMP1 trafficking, such as the existence of a soluble, chaperoned trafficking state that is not fully folded? Was a PfEMP1-BPTI fusion ever tested as an alternative to mDHFR?

This is an interesting suggestion. The PfEMP1-BPTI was never tested. However, a chaperoned trafficking state would likely also affect BPTI. Given that both domains (mDHFR and BPTI) in principle do the same when folded and would block when the construct is in the PV, it is not so likely that using a different blocking domain would make a difference. Therefore, the scenario where BPTI would block when mDHFR does not, is not that probable. The opposite would be possible (mDHFR blocking while BPTI does not, because only the latter depends on the redox state). However, this would only happen if the block  occurred before the construct reaches the PV.

At present, we believe the lacking block to be due to the organization of the domains in the construct. In the PfEMP1-mDHFR construct in this manuscript the position of the blocking domain is further away from the TMD compared to all other previously tested mDHFR fusions. Increased distance to the TMD has previously been found to be a factor impairing the blocking function of mDHFR (Mesen-Ramirez et al., PlosPath 2016 (PMID: 27168322)). Hence, our suspicion that this is the reason for the lacking block with the PfEMP1-mDHFR rather than the type of blocking domain. However, the latter option can’t be fully excluded and we might test BPTI in future work.

(3) The late promoter SBP1-mDHFR is 2A fused with the KAHRP reporter. Since 2A skipping efficiency varies between fusion contexts and significant amounts of unskipped protein can be present, it would be helpful to include a WB to determine the efficiency of skipping and provide confidence that the co-blocked KAHRP in the +WR condition (Fig 2D) is not actually fused to the C-terminus of SBP1-mDHFR-GFP.

Fortunately, this T2A fusion (crt_SBP1-mDHFR-GFP-2A-KAHRP-mScarlet^epi) was used before in work that included a Western blot showing its efficient skipping (S3 A Fig in MesenRamirez et al., PlosPath 2016). In agreement with these Western blot result, fluorescence microscopy showed very limited overlap of SBP1-mDHFR-GFP and KAHRP-mCherry in absence of WR (Fig. 3B in Mesen-Ramirez et al., PlosPath 2016 and Fig. 2 in this manuscript) which would not be the case if these two constructs were fused together. Please note that KAHRP is known to transiently localize to the Maurer’s clefts before reaching the knobs (Wickham et al., EMBOJ 2001, PMID: 11598007), and therefore occasional overlap with SBP1 at the Maurer’s clefts is expected. However, we would expect much more overlap if a substantial proportion of the construct population would not be skipped and therefore the co-blocked KAHRP-mCherry in the +WR sample is unlikely to be due to inefficient skipping and attachment to SBP1-mDHFR-GFP.

(4) Does comparison of RNAseq from the various 3D7 and IT4 lines in the study provide any insight into PTP3 expression levels between strains with different binding capacities? Was the expression level of ptp3a/b in the IT4var19 panned line similar to the expression in the parent or other activated IT4 lines? Could the expanded ptp3 gene number in IT4 indicate that specialized trafficking machinery exists for some PfEMP1 proteins (ie, IT4var19 requires the divergent PTP3 paralog for efficient trafficking)?

PTP3 in the different IT4 lines that bind:

In those parasite lines that did bind, the intrinsic variation in the binding assays, the different binding properties of different PfEMP1 variants and the variation in RNA Seq experiments to compare different parasite lines precludes a correlation of binding level vs ptp3 expression. For instance, if a PfEMP1 variant has lower binding capacity, ptp3 may still be higher but binding would be lower than if comparing to a parasite line with a better binding PfEMP1 variant. Studying the effect of PTP3 levels on binding could probably be done by overexpressing PTP3 in the same PfEMP1 SLI expressor line and assessing how this affects binding, but this would go beyond this manuscript.

PTP3 in panned vs unpanned Var19:

We did some comparisons between IT4 parent, and the IT4-Var19 panned and unpanned

(see Author response table 1). This did not reveal any clear associations. While the parent had somewhat lower ptp3 transcript levels, they were still clearly higher than in the unpanned Var19 line and other lines had also ptp3 levels comparable to the panned IT4-Var19 (see Author response table 2) 

PTP3 in the TGDs and possible reason for binding phenotype:

A key point is whether PTP3 could have influenced the lack of binding in the TGD lines (see also weakness section and point 1 of public review of reviewer 3: ptp3 may be an indirect cause resulting in lacking binding in TGD parasites). We now did RNA Seq to check for ptp3 expression in the relevant TGD lines although we did not do a systematic quantitative comparison (which would require 3 replicates of RNASeq), but we reasoned that loss of expression would also be evident in one replicate. There was no indication that the TGD lines had lost PTP3 expression (see Author response table 2) and this is unlikely to explain the binding loss in a similar fashion to the Var19 parasites. Generally, the IT4 lines showed expression of both ptp3 genes and only in the Var19 parasites before panning were the transcript levels considerably lower:

Author response table 1.

Parent vs IT4-Var19 panned and unpanned

Author response table 2.

TGD lines with binding phenotype vs parent

The absence of an influence of PTP3 on the binding phenotype in the cell lines in this manuscript (besides Var19) is further supported by its role in PfEMP1 surface display. Previous work has shown that KO of ptp3 leads to a loss of VAR2CSA surface display (Maier et al., Cell 2008). The unpanned Var19 parasite also lacked PfEMP1 surface display and panning and the resulting appearance of the binding phenotype was accompanied by surface display of PfEMP1. As both, the EMPIC3 and TryThra-TGD lines had still at least some PfEMP1 on the surface, this also (in addition to the RNA Seq above) speaks against PTP3 being the cause of the binding phenotype. The same applies to 3D7 which despite the poor binding displays PfEMP1 on the host cell surface (Figure 1D). This indicating that also the binding phenotype in 3D7 is not due to PTP3 expression loss, as this would have abolished PfEMP1 surface display. 

The idea about PTP3 paralogs for specific PfEMP1s is intriguing. In the future it might be interesting to test the frequency of parasites with two PTP3 paralogs in endemic settings and correlate it with the PfEMP1 repertoire, variant expression and potentially disease severity. 

(5) The IT4var01 line shows substantially lower binding in Figure 5F compared with the data shown in Figure 4E and 6F. Does this reflect changes in the binding capacity of the line over time or is this variability inherent to the assay?

There is some inherent variability in these assays. While we did not systematically assess this, we had no indication that this was due to the parasite line changing. The Var01 line was cultured for months and was frozen down and thawed more than once without a clear gradual trend for more or less binding. While we can’t exclude some variation from the parasite side, we suspect it is more a factor of the expression of the receptor on the CHO cells the iRBCs bind to. 

Specifically, the assays in Fig. 6F and 4E mentioned by the reviewer both had an average binding to CD36 of around 1000 iE/mm2, only the experiments in Fig. 5F are different (~ 500 iE/mm2) but these were done with a different batch of CHO cells at a different time to the experiments in Fig. 6F and 4E. 

(6) In Figure S7A, TryThrA and EMPIC3 show distinct localization as circles around the PfEMP1 signal while PeMP2 appears to co-localize with PfEMP1 or as immediately adjacent spots (strong colocalization is less apparent than SBP1, and the various PfEMP1 IFAs throughout the study). Does this indicate that TryThrA and EMPIC3 are peripheral MC proteins? Does this have any implications for their function in PfEMP1 binding? Some discussion would help as these differences are not mentioned in the text. For the EMPIC3 TGD IFAs, localization of SBP1 and PfEMP1 is noted to be normal but REX1 is not mentioned (although this also appears normal).

We apologise for the lacking description of the candidate localisations and cursory description of the Maurer’s clefts phenotypes (next point). Our original intent was to not distract too much from the main flow of the manuscript as almost every part of the manuscript could be followed up with more details. However, we fully agree that this is unsatisfactory and now provided more description (this point) and more data (next point).

Localisation of TryThrA and EMPIC3 compared to PfEMP1 at the Maurer’s clefts: the circular pattern is reminiscent of the results with Maurer’s clefts proteins reported by McMillan et al using 3D-SIM in 3D7 parasites (McMillan et al., Cell Microbiology 2014 (PMID: 23421990)). In that work SBP1 and MAHRP1 (both integral TMD proteins) were found in foci but REX1 (no TMD) in circular structures around these foci similar to what we observed here for TryThrA and EMPIC3 which both also lack a TMD. The SIM data in McMillan et al indicated that also PfEMP1 is “more peripheral”, although it did only partially overlap with REX1. The conclusion from that work was that there are sub-compartments at the Maurer’s clefts. In our IFAs (Fig. S7A) PfEMP1 is also only partially overlapping with the TryThrA and EMPIC3 circles, potentially indicating similar subcompartments to those observed by 3D-SIM. We agree with the reviewer that this might be indicative of peripheral MC proteins, fitting with a lack of TMD in these candidates, but we did not further speculate on this in the manuscript.

We now added enlargements of the ring-like structures to better illustrate this observation in Fig. S7A. In addition, we now specifically mention the localization data and the ring like signal with TryThrA and EMPIC3 in the results and state that this may be similar to the observations by McMillan et al., Cell Microbiology 2014.

We also thank the reviewer for pointing out that we had forgotten to mention REX1 in the EMPIC3-TGD, this was amended.  

(7) The atypical localization in TryThrA TGD line claimed for PfEMP1 and SBP1 in Fig S7B is not obvious. While most REX1 is clustered into a few spots in the IFA staining for SBP1 and REX1, SBP1 is only partially located in these spots and appears normal in the above IFA staining for SBP1 and HA. The atypical localization of PfEMP1-HA is also not obvious to me. The authors should clarify what is meant by "atypical" localization and provide support with quantification given the difference between the two SBP1 images shown.

We apologise for the inadequate description of these IFA phenotypes. The abnormal signal for SBP1, REX1 and PfEMP1 in the TryThrA-TGD included two phenotypes found with all 3 proteins: 

(1) a dispersed signal for these proteins in the host cell in addition to foci (the control and the other TGD parasites have only dots in the host cell with no or very little detectable dispersed signal). 

(2) foci of disproportionally high intensity and size, that we assumed might be aggregation or enlargement of the Maurer’s clefts or of the detected proteins.

The reason for the difference between the REX1 (aggregation) phenotype and the PfEMP1 and SBP1 (dispersed signal, more smaller foci) phenotypes in the images in Fig. S7B is that both phenotypes were seen with all 3 proteins but we chose a REX1 stained cell to illustrate the aggregation phenotype (the SBP1 signal in the same cell is similar to the REX1 signal, illustrating that this phenotype is not REX1 specific; please note that this cell also has a dispersed pool of REX1 and SBP1). 

Based on the IFAs 66% (n = 106 cells) of the cells in the TryThrA-TGD parasites had one or both of the observed phenotypes. We did not include this into the previous version of the manuscript because a description would have required detouring from the main focus of this results section. In addition, IFAs have some limitations for accurate quantifications, particularly for soluble pools (depending on fixing efficiency and agent, more or less of a soluble pool in the host cell can leak out). 

To answer the request to better explain and quantify the phenotype and given the limitations of IFA, we now transfected the TryThrA-TGD parasites with a plasmid mediating episomal expression of SBP1-mCherry, permitting live cell imaging and a better classification of the Maurer’s clefts phenotype. Due to the two SLI modifications in these parasites (using up 4 resistance markers) we had to use a new selection marker (mutated lactate transporter PfFNT, providing resistance to BH267.meta (Walloch et al., J. Med. Chem. 2020 (PMID: 32816478))) to transfect these parasites with an additional plasmid. 

These results are now provided as Fig. S8 and detailed in the last results section. The new data shows that the majority of the TryThrA-TGD parasites contain a dispersed pool of SBP1 in the host cell. About a third of the parasites also showed disproportionally strong SBP1 foci that may be aggregates of the Maurer’s clefts. We also transfected the EMPIC3-TGD parasites with the FNT plasmid mediating episomal SBP1-mCherry expression and observed only few cells with a cytoplasmic pool or aggregates (Fig. S8). Overall these findings agree with the previous IFA results. As the IFA suggests similar results also for REX1 and PfEMP1, this defect is likely not SBP1 specific but more general (Maurer’s clefts morphology; association or transport of multiple proteins to the Maurer’s clefts). This gives a likely explanation for the cytoadherence phenotype in the TryThrA-TGD parasites. The reason for the EMPIC3-TGD phenotype remains to be determined as we did not detect obvious changes of the Maurer’s clefts morphology or in the transport of proteins to these structures in these experiments. 

Minor comments

(1) Italicized numbers in parenthesis are present in several places in the manuscript but it is not clear what these refer to (perhaps differently formatted citations from a previous version of the manuscript). Figure 1

legend: (121); Figure S3 legend: (110), (111); Figure S6 legend: (66); etc.

We thank the reviewer for pointing out this issue with the references, this was amended.

(2) Figure 5A and legend: "BSD-R: BSD-resistance gene". Blasticidin-S (BS) is the drug while Blasticidin-S deaminase (BSD) is the resistance gene.

We thank the reviewer for pointing this out, the legend and figure were changed.

(3) Figure 5E legend: µ-SBP1-N should be α-SBP1-N.

This was amended.

(4) Figure S5 legend: "(Full data in Table S1)" should be Table S3.

This was amended.

(5) Figure S1G: The pie chart shows PF3D7_0425700 accounts for 43% of rif expression in 3D7var0425800 but the text indicates 62%.

We apologize for this mistake, the text was corrected. We also improved the citations to Fig. S1G and H in this section.

(6) "most PfEMP1-trafficking proteins show a similar early expression..." The authors might consider including a table of proteins known to be required for EMP1 trafficking and a graph showing their expression timing. Are any with later expressions known?

Most exported proteins are expressed early, which is nicely shown in Marti et al 2004 (cited for the statement) in a graph of the expression timing of all PEXEL proteins (Fig. 4B in that paper). PNEPs also have a similar profile (Grüring et al 2011, also cited for that statement), further illustrated by using early expression as a criterion to find more PNEPs (Heiber et al., 2013 (PMID: 23950716)). Together this includes most if not all of the known PfEMP1 trafficking proteins. The originally co-submitted paper (Blancke-Soares & Stäcker et al., eLife preprint doi.org/10.7554/eLife.103633.1) analysed several later expressed exported proteins

(Pf332, MSRP6) but their disruption, while influencing Maurer’s clefs morphology and anchoring, did not influence PfEMP1 transport. However, there are some conflicting results for Pf332 (referenced in Blancke-Soares & Stäcker et al). This illustrates that it may not be so easy to decide which proteins are bona fide PfEMP1 trafficking proteins. We therefore did not add a table and hope it is acceptable for the reader to rely on the provided 3 references to back this statement.

(7)  Figure S1J: The predominate var in the IT4 WT parent is var66 (which appears to be syntenic with Pf3D7_0809100, the predominate var in the 3D7 WT parent). Is there something about this locus or parasite culture conditions that selects for these vars in culture? Is this observed in other labs as well?

This is a very interesting point (although we are not certain these vars are indeed syntenic, they are on different chromosomes). As far as we know at least Pf3D7_0809100 is commonly a dominant var transcribed in other labs and was found expressed also in sporozoites (Zanghì et al. Cell Rep. 2018). However, it is unclear how uniform this really is. For IT4 we do not know in full but have also here commonly observed centromeric var genes to be dominating transcripts in unselected parasite cultures. It is possible that transcription drifts to centromeric var genes in cultured parasites. However, given the anecdotal evidence, it is unknown to which extent this is related to an inherent switching and regulation regiment or a consequence of faulty regulation following prolonged culturing.

(8) Figure 4B, C: Presumably the asterisks on the DNA gels indicate non-specific bands but this is not described in the legend. Why are non-specific bands not consistent between parent and integrated lanes?

We apologize for not mentioning this in the legend, this was amended.

It is not clear why the non-specific bands differ between the lines but in part this might be due to different concentrations and quality of DNA preps. A PCR can also behave differently depending on whether the correct primer target is present or not. If present, the PCR will run efficiently and other spurious products will be outcompeted, but in absence of the correct target, they might become detectable.  

Overall, we do not think the non-specific bands are indications of anything untoward with the lines, as for instance in Fig. 4B the high band in the 5’ integration in the IT4 line (that does not occur anywhere else) can’t be due to a genomic change as this is the parental line and does not contain the plasmid for integration. In the same gel, the ori locus band of incorrect size (likely due to crossreaction of the primers to another var gene which due to the high similarity of the ATS region is not always fully avoidable), is present in both, the parent IT4 and the integrant line which therefore also is not of concern. In C there are a couple of bands of incorrect size in the Integration line. One of these is very faint and both are too large and again therefore are likely other vars that are inefficiently picked up by these primers. The reason they are not seen in the parent line is that there the correct primer binding site is present, which then efficiently produces a product that outcompetes the product derived from non-optimal matching primer products and hence appear in the Int line where the correct match is not there anymore. For these reasons we believe these bands are not of any concern.  

(9) Figure 4C: Is there a reason KAHRP was used as a co-marker for the IFA detecting IT4var19 expression instead of SBP1 which was used throughout the rest of the study?

This is a coincidence as this line was tested when other lines were tested for KAHRP. As there were foci in the host cell we were satisfied that the HA-tagged PfEMP1 is produced and the localization deemed plausible. 

(10) Figure 6: Streptavidin labeling for the IT4var01-BirA position 3 line is substantially less than the other two lines in both IFA and WB. Does the position 3 fusion reduce PfEMP1 protein levels or is this a result of the context or surface display of the fusion? Interestingly, the position 3 trypsin cleavage product appears consistently more robust compared with the other two configurations. Does this indicate that positioning BirA upstream of the TM increases RBC membrane insertion and/or makes the surface localized protein more accessible to trypsin?

It is possible that RBC membrane insertion or trypsin accessibility is increased for the position 3 construct. But there could also be other explanations:

The reason for the more robustly detected protected fragment for the position 3 construct in the WB might also be its smaller size (in contrast to the other two versions, it does not contain BirA*) which might permit more efficient transfer to the WB membrane. In that case the more robust band might not (only) be due to better membrane insertion or better trypsin accessibility.

The lower biotinylation signal with the position 3 construct might also be explained by the farther distance of BirA* to the ATS (compared to position 1 and 2), the region where interactors are expected to bind. The position 1 and 2 constructs may therefore generally be more efficient (as closer) to biotinylate ATS proximal proteins. Further, in the final destination (PfEMP1 inserted into the RBC membrane) BirA* would be on the other side of the membrane in the position 3 construct while in the position 1 and 2 constructs BirA* would be on the side of the membrane where the ATS anchors PfEMP1 in the knob structure. In that case, labelling with position 3 would come from interactions/proximities during transport or at the Maurer’s clefts (if there indeed PfEMP1 is not membrane embedded) and might therefore be less.

Hence, while alterations in trypsin accessibility and RBC membrane insertion are possible explanations, other explanations exist. At present, we do not know which of these explanations apply and therefore did not mention any of them in the manuscript. 

Reviewer #3 (Recommendations for the authors):

(1) In the abstract and on page 8, the authors mention that they generate cell lines binding to "all major endothelial receptors" and "all known major receptors". This is a pretty allencompassing statement that might not be fully accepted by others who have reported binding to other receptors not considered in this paper (e.g. VCAM, TSP, hyaluronic acid, etc). It would be better to change this statement to something like "the most common endothelial receptors" or "the dominant endothelial receptors", or something similar.

We agree with the reviewer that these statements are too all-encompassing and changed them to “the most common endothelial receptors” (introduction) and “the most common receptors” (results).

(2) The authors targeted two rif genes for activation and in each case the gene became the most highly expressed member of the family. However, unlike var genes, there were other rif genes also expressed in these lines and the activated copy did not always make up the majority of rif mRNAs. The authors might wish to highlight that this is inconsistent with mutually exclusive expression of this gene family, something that has been discussed in the past but not definitively shown.

We thank the reviewer for highlighting this, we now added the following statement to this section: “While SLI-activation of rif genes also led to the dominant expression of the targeted rif gene, other rif genes still took up a substantial proportion of all detected rif transcripts, speaking against a mutually exclusive expression in the manner seen with var genes.”

(3) In Figure 6, H-J, the authors display volcano plots showing proteins that are thought to interact with PfEMP1. These are labeled with names from the literature, however, several are named simply "1, 2, 3, 4, 5, or 6". What do these numbers stand for?

We apologize for not clarifying this and thank the reviewer for pointing this out. There is a legend for the numbered proteins in what is now Table S4 (previously Table S3). We now amended the legend of Figure 6 to explain the numbers and pointing the reader to Table S4 for the accessions.

very important to keep in mind because sometimes we think that our personal experiences aren't relatable.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

Colorectal cancer (CRC) is the third most common cancer globally and the second leading cause of cancer-related deaths. Colonoscopy and fecal immunohistochemical testing are among the early diagnostic tools that have significantly enhanced patient survival rates in CRC. Methylation dysregulation has been identified in the earliest stages of CRC, offering a promising avenue for screening, prediction, and diagnosis. The manuscript entitled "Early Diagnosis and Prognostic Prediction of Colorectal Cancer through Plasma Methylation Regions" by Zhu et al. presents that a panel of genes with methylation pattern derived from cfDNA (27 DMRs), serving as a noninvasive detection method for CRC early diagnosis and prognosis.

Strengths:

The authors provided evidence that the 27 DMRs pattern worked well in predicting CRC distant metastasis, and the methylation score remarkably increased in stage III-IV.

Weaknesses:

The major concerns are the design of DMR screening, the relatively low sensitivity of this DMR pattern in detecting early-stage CRC, the limited size of the cohorts, and the lack of comparison with the traditional diagnosis test.

We sincerely thank the reviewer for their thorough evaluation and constructive feedback on our manuscript. We are encouraged that the reviewer found our 27-DMR panel promising for predicting distant metastasis and for its performance in late-stage CRC. We have carefully considered the weaknesses pointed out and have made revisions to address these concerns, which we believe have significantly strengthened our paper.

We agree with the reviewer that achieving high sensitivity for early-stage disease is the ultimate goal for any noninvasive screening test. Detecting the minute quantities of cfDNA shed from early-stage tumors is a well-recognized challenge in the field. Although the sensitivity of our current panel for early-stage CRC is modest, its core strengths, lie in its capability to also detect advanced adenomas and its excellent performance in assessing CRC metastasis and prognosis. Furthermore, we have now added a direct comparative analysis of our 27-DMR panel against the most widely used clinical serum biomarker for CRC, carcinoembryonic antigen (CEA), using samples from the same patient cohorts. Our results demonstrate that 27-DMR methylation score significantly outperforms CEA in diagnostic accuracy for early-stage CRC (64% vs. 18%) (Table s7). And in the Discussion section, we have also acknowledged our limitations and suggest that future studies are warranted to combine the cfDNA methylation model with commonly used clinical markers, such as CEA and CA19-9, with the aim of improving the sensitivity for early diagnosis.

We acknowledge the reviewer's concern regarding the cohort size and validation in larger, prospective, multi-center cohorts is essential before this panel can be considered for clinical application. We have explicitly stated this as a limitation of our study in the Discussion section and have highlighted the need for future large-scale validation studies (Page 18, Lines 367-373). We once again thank the reviewer for their insightful comments, which have allowed us to substantially improve our manuscript. We hope that the revised version is now suitable for publication.

Reviewer #2 (Public review):

This work presents a 27-region DMR model for early diagnosis and prognostic prediction of colorectal cancer using plasma methylation markers. While this non-invasive diagnostic and prognostic tool could interest a broad readership, several critical issues require attention.

Major Concerns:

(1) Inconsistencies and clarity issues in data presentation

(a) Sample size discrepancies

The abstract mentions screening 119 CRC tissue samples, while Figure 1 shows 136 tissues. Please clarify if this represents 119 CRC and 17 normal samples.

We sincerely thank the reviewer for this careful observation and for pointing out the inconsistency. We apologize for the error and the confusion it caused. Regarding Figure 1: The reviewer is correct. The number 136 in the original Figure 1 was an error. This was due to an inadvertent double-counting of the tumor samples that were used in the differential analysis against adjacent normal tissues. The actual number of tissue samples used in this analysis is 89. We have now corrected this value in the revised Figure 1.

Regarding the Abstract: The 119 CRC tissue samples mentioned in the abstract represents the total number of unique tumor samples analyzed across all stages of our study. This number is composed of two cohorts: the initial 15 pairs of tissues used for preliminary screening, and the subsequent 89 tissue samples used for validation, totaling 119 samples. We have ensured all sample numbers are now consistent throughout the revised manuscript.

The plasma sample numbers vary across sections: the abstract cites 161 samples, Figure 1 shows 116 samples, and the Supplementary Methods mentions 77 samples (13 Normal, 15 NAA, 12 AA, 37 CRC).

We sincerely thank the reviewer for their meticulous review and for identifying these inconsistencies in the plasma sample numbers. We apologize for this oversight and the lack of clarity.

Figure 1 & Supplementary Methods (77 samples): The number 116 in the original Figure 1 was a clerical error. The correct number is 77, which is the cohort used for our differential methylation analysis. This number is now consistent with the Supplementary Methods. This cohort is composed of 13 Normal, 15 NAA, 12 AA, and 37 CRC samples. The figure has been revised accordingly.

Abstract (161 samples): The total of 161 plasma samples mentioned in the abstract is the sum of two distinct sample sets used for different stages of our analysis: The 77 samples (13 Normal, 15 NAA, 12 AA, 37 CRC) used for the differential analysis.  An additional 84 samples (33 Normal, 51 CRC) which served as the training set for the LASSO regression model. We have now clarified these distinctions in the text and ensured consistency across the abstract, figures, and methods sections.

(b) Methodological inconsistencies

The Supplementary Material reports 477 hypermethylated sites from TCGA data analysis (Δβ>0.20, FDR<0.05), but Figure 1 indicates 499 sites.

The manuscript states that analyzing TCGA data across six cancer types identified 499 CRC-specific methylation sites, yet Figure 1 shows 477. Please also explain the rationale for selecting these specific cancer types from TCGA.

We sincerely thank the reviewer for their sharp observation and for highlighting these inconsistencies. We apologize for this clerical error, which occurred when labeling the figure. The numbers 477 and 499 in Figure 1 were inadvertently swapped and the text in Supplementary Material is correct. We have now corrected this error throughout the manuscript to ensure clarity and consistency. We deeply regret the confusion this has caused.

Regarding the rationale for selecting the cancer types:

The selection of colorectal, esophageal, gastric, lung, liver, and breast cancers was based on the following strategic criteria to ensure the stringent identification of CRC-specific markers. Firstly, esophageal, gastric, liver, and colorectal cancers all originate from the gastrointestinal tract and share developmental and functional similarities. Comparing CRC against these closely related cancers allowed us to filter out general GI-tract-related methylation patterns and isolate those that are truly unique to colorectal tissue. Secondly, we included lung and breast cancer as they are two of the most common non-GI malignancies worldwide with distinct tissue origins. This helps ensure our identified markers are not just pan-cancer methylation events but are specific to CRC, even when compared against highly prevalent cancers from different lineages. Finally, these six cancer types have some of the largest and most complete datasets available in the TCGA database, including high-quality methylation data. This provided a robust statistical foundation for a reliable cross-cancer comparison. We hope this explanation clarifies our methodology. Thank you again for your valuable feedback.

"404 CRC-specific DMRs" mentioned in the main text while "404 MCBs" in Figure 1, the authors need to clarify if these terms are interchangeable or how MCBs are defined.

We sincerely thank the reviewer for pointing out this important inconsistency in terminology. We apologize for the confusion this has caused and for the error in Figure 1. The two terms are closely related in our study. The final 404 markers are technically DMRs that were identified through an analysis of MCBs. To avoid confusion, we have decided to unify the terminology. The manuscript has now been revised to consistently use "DMRs", which is the most accurate final descriptor. The label in Figure 1 has been corrected accordingly.

(2) Methodological documentation

The Results section requires a more detailed description of marker identification procedures and justification of methodological choices.

Figure 3 panels need reordering for sequential citation.

We thank the reviewer for this valuable suggestion. We agree that the original Results section lacked sufficient detail regarding the marker identification procedures and the justification for our methodological choices. To address this, we have substantially rewritten the "Methylation markers selection" subsection. This revised section provides a clear, step-by-step narrative of our marker discovery. The revised text now integrates the specific methodological details and statistical criteria. For instance, we now explicitly describe the three-pronged approach for the initial TCGA data mining and the specific criteria (Δβ, FDR, log2FC) for each, and the analysis methodology such as Wilcoxon test and LASSO regression analysis. We believe this detailed narrative now provides the necessary description and justification for our methodological choices directly within the results, significantly improving the clarity and logical flow of our manuscript. This revision can be found on (Page 9-11, Lines 180-195, 202-213). We hope these changes fully address the reviewer's concerns.

We thank the reviewer for pointing out the citation order of the panels in Figure 3. This was a helpful suggestion for improving the clarity of our manuscript. We have now reordered the panels in Figure 3 to ensure they are cited sequentially within the text. These adjustments have been made in the "Development and validation of the CRC diagnosis model" subsection of the Results (Page 11, lines 224-230). We appreciate the reviewer's attention to detail.

(3) Quality control and data transparency

No quality control metrics are presented for the in-house sequencing data (e.g., sequencing quality, alignment rate, BS conversion rate, coverage, PCA plots for each cohort).

The analysis code should be publicly available through GitHub or Zenodo.

At a minimum, processed data should be made publicly accessible to ensure reproducibility.

We sincerely thank the reviewer for their valuable and constructive feedback regarding quality control and data transparency. We fully agree that these elements are crucial for ensuring the robustness and reproducibility of our research. As the reviewer suggested, we have made all processed data and the key quality control metrics for each sample including sequencing quality scores, bisulfite (BS) conversion rates, and sequencing coverage publicly available to ensure the reproducibility of our findings. The analysis was performed using standard algorithms as detailed in the Methods section. While we are unable to host the code in a public repository at this time, all analysis scripts are available from the corresponding author upon reasonable request. The data has been deposited in the National Genomics Data Center (NGDC) and is accessible under the accession number OMIX009128. This information is now clearly stated in the "Data and Code Availability" section of the manuscript. We thank the reviewer again for pushing us to improve our manuscript in this critical aspect.

Reviewer #3 (Public review):

Summary:

This article provides a model for early diagnosis and prognostic prediction of Colorectal Cancer and demonstrates its accuracy and usability. However, there are still some minor issues that need to be revised and paid attention to.

Strengths:

A large amount of external datasets were used for verification, thus demonstrating robustness and accuracy. Meanwhile, various influencing factors of multiple samples were taken into account, providing usability.

Weaknesses:

There are notable language issues that hinder readability, as well as a lack of some key conclusions provided.

We are very grateful to the reviewer for their positive assessment of our study and for the constructive feedback provided. We are particularly encouraged that the reviewer recognized the strengths of our work, especially the robustness demonstrated through extensive external validation and the practical usability of our model. Regarding the weaknesses, we have taken the comments very seriously and have thoroughly revised the manuscript. We sincerely apologize for the language issues that hindered readability in our initial submission. To address this, the entire manuscript has undergone a comprehensive round of professional language polishing and editing. We have carefully reviewed and revised the text to improve clarity, flow, and grammatical accuracy. Besides, we agree that the conclusions could be stated more explicitly. To rectify this, we have substantially revised the final paragraph of the Discussion and the Conclusion section (Page 14-18, lines 279-305, 319-334, 346-348, 358-360, 367-379). We now more clearly summarize the main findings of our study, emphasize the clinical significance and potential applications of our model, and provide clear take-home messages. We thank you again for your time and insightful comments, which have been invaluable in improving the quality of our paper. We hope the revised manuscript now meets the standards for publication.

Reviewer #1 (Recommendations for the authors):

Detail comments are outlined below:

(1) In this study, the authors have highlighted methylated cfDNA as a noninvasive approach for CRC early diagnosis. However, the small size of cohorts for plasma screening, particularly the sample number of NAA and AA , may cause bias in the selection of DMRs. This bias may lead to inappropriate DMRs for early diagnosis. Furthermore, the similar issues for the training set with a high percentage of late-stage CRC, no AA or NAA samples were included. This absence may be the key factor in screening changed methylated cfDNA that can predict the early stages of CRC.

We are very grateful to the reviewer for this insightful methodological critique. We agree that cohort composition and sample size are critical factors in the development of robust biomarkers, and we appreciate the opportunity to clarify our study design and the interpretation of our results.

We agree with the reviewer that the number of precancerous lesion samples (NAA and AA) in our initial plasma screening cohort was limited. This is a valid point. However, it is important to contextualize the role of this step within our overall multi-stage marker selection funnel. The markers evaluated in this plasma cohort were not discovered from this small sample set alone. They were the result of a rigorous pre-selection process based on large-scale public TCGA data and our own tissue-level sequencing. This robust, tissue-based validation ensured that only the most promising CRC-specific markers were advanced for plasma testing. Therefore, while the plasma cohort was modest in size, its purpose was to confirm the circulatory detectability of markers already known to have a strong tissue-of-origin signal, thereby mitigating the potential bias from a smaller discovery set.

Our primary aim was to first build a model that could robustly and accurately identify a definitive cancer-specific methylation signal. By training the model on clear-cut invasive cancer cases versus healthy controls, we could isolate the most powerful and specific markers for established malignancy. Our working hypothesis was that these strong cancer-specific methylation patterns are initiated during the precursor stages and would therefore be detectable, albeit at lower levels, in precancerous lesions.  Unfortunately, the panel could only identify a limited proportion of precancerous lesions (48.4% in the NAA group and 52.2% in the AA group). We fully agree with the reviewer's sentiment that including a larger and more balanced set of precancerous lesions in future training cohorts could potentially optimize a model specifically for adenoma detection. We have now explicitly added this point to our Discussion section, highlighting it as an important direction for future research (Page 18, lines 367-373).

(2) The sensitivity of 27 DMRs in the external validation set (for NAA, AA and CRC 0-Ⅱare 48.4%. 52.2% and 66.7%, respectively) were much lower compared with previously published studies, like ColonES assay (DOI: 10.1016/j.eclinm.2022.101717) and ColonSecure test (DOI: 10.1186/s12943-023-01866-z). The 27 DMRs from the layered screening process did not show superior performance in a small population of an external validation cohort. Therefore, it is unlikely that this DMR pattern will be applicable to the general population in the future.

We sincerely thank the reviewer for their insightful comments and for providing a thorough comparison with the highly relevant ColonES and ColonSecure assays. This has given us an important opportunity to clarify the unique contributions and specific clinical applications of our 27-DMR panel.

We acknowledge the reviewer's point that the sensitivities of our panel for precancerous lesions (NAA: 48.4%, AA: 52.2%), while substantial, are numerically lower than those reported by the excellent ColonES assay (AA: 79.0%). However, it is important to clarify that while the ColonES and ColonSecure tests are outstanding benchmarks designed primarily for early detection and screening, the primary objective and contribution of our study were slightly different. Our model demonstrated an exceptional ability to predict distant metastasis with an AUC of 0.955 and a strong capacity for predicting overall prognosis with an AUC of 0.867. Our goal was to develop a multi-functional, biologically-rooted biomarker panel that not only contributes to early detection but, more importantly, provides crucial information for post-diagnosis patient management, including staging, risk stratification, and prognostication, from a single preoperative sample. We believe this ability to preoperatively identify high-risk patients who may require more aggressive treatment or intensive surveillance is the key contribution of our work. It provides a distinct clinical utility that complements, rather than directly competes with, pure screening assays.

We agree with the reviewer that our external validation was performed on a limited cohort, and we have acknowledged this as a limitation in our Discussion section. However, the purpose of this validation was to provide a proof-of-concept for the panel's performance across its multiple functions. The promising and exceptionally high-performing results in the prognostic domain strongly warrant further validation in larger, prospective, multi-center cohorts.

(3) The 27 DMRs pattern worked well in predicting CRC distant metastasis, and the methylation score remarkably increased in stage III-IV. In contrast, the increase of AA and 0-II groups was very mild in the validation cohort. This observation raises concerns regarding the study design, particularly in the context of the layered screening process and sample assigning.

We sincerely thank the reviewer for this insightful and critical comment. We agree with the reviewer's observation that the methylation score increased more remarkably in late-stage (III-IV) CRC compared to the milder increase in adenoma (AA) and early-stage (0-II) CRC in the validation cohort. However, the observed pattern is biologically plausible and consistent with the nature of colorectal cancer progression. Carcinogenesis is a multi-step process involving the gradual accumulation of genetic and epigenetic alterations. The methylation changes we identified are likely associated with tumor progression and metastasis. Therefore, it is expected that advanced, metastatic cancers (Stage III-IV), which have undergone significant biological changes, would exhibit a much stronger and more robust methylation signal compared to pre-cancerous lesions (adenomas) or early-stage, non-metastatic cancers (Stage 0-II). The "mild" increase in early stages reflects the initial, more subtle epigenetic alterations, while the "remarkable" increase in late stages reflects the extensive changes required for invasion and metastasis. We believe this graduated increase actually strengthens the validity of our methylation signature, as it mirrors the underlying biological progression of the disease. We hope this response and the corresponding revisions address the reviewer's comments.

(4) The authors did not provide the 27 DMRs prediction efficacy comparison with other noninvasive CRC assays, like a CEA and a FIT test.

Thank you for this valuable suggestion. We agree that comparing our model with established non-invasive assays is crucial for demonstrating its clinical potential. Following your advice, we have now included a direct comparison of the diagnostic performance between our model and the traditional tumor marker, carcinoembryonic antigen (CEA), using the external validation cohort. The results show that our model has a significantly higher sensitivity for detecting early-stage colorectal cancer and adenomas compared to CEA. This detailed comparison has been added as Table s7 in the supplementary materials, and the corresponding description has been incorporated into the Results section of our manuscript (Page 12, lines 234-236). Regarding the Fecal Immunochemical Test (FIT), we unfortunately could not perform a direct statistical comparison because very few individuals in our cohort had undergone FIT. A comparison based on such a small sample size would lack statistical power and might not yield meaningful conclusions. We have acknowledged this as a limitation of our study in the Discussion section.We believe these additions and clarifications have substantially strengthened our manuscript. Thank you again for your constructive feedback.

(5) The authors did not explicitly describe how they assigned the plasma samples to the distinct sets, nor did they specify the criteria for the plasma screen set, training set, and validation set. The detailed information for the patient grouping should be listed.

Responce: Thank you for this essential feedback. We agree that a transparent and detailed description of the sample allocation process is crucial for the manuscript. We apologize for the previous lack of clarity and have now revised the Methods section to address this. Our patient cohorts were assigned to the screening, training, and validation sets based on a chronological splitting strategy. Specifically, samples were allocated based on the date of collection in a consecutive manner. This approach was chosen to minimize selection bias and to provide a more realistic, forward-looking assessment of the model's performance, simulating a prospective validation scenario. The screening set comprised 89 tissue samples and 77 plasma samples collected between June to December 2020. The primary purpose of this set was for the initial discovery and screening of potential methylation markers. The training set and validation set included 165 plasma samples collected from December 2020 to July 2022. The external validation cohort comprised 166 plasma samples collected from from July 2022 to December 2022. The subsection titled "Study design and samples" within the Methods section of the revised manuscript, which now contains all of this detailed information (Page 6, lines 116-133). We believe this detailed explanation now makes our study design clear and transparent. Thank you again for helping us improve our manuscript.

Reviewer #2 (Recommendations for the authors):

The manuscript requires significant language editing to improve clarity and readability. We recommend that the authors seek professional editing services for revision.

Thank you for your constructive comments on the language of our manuscript. We apologize for any lack of clarity in the previous version. To address this, we have performed a thorough revision of the manuscript. The text has been carefully reviewed and edited by a native English-speaking colleague who is an expert in our research field. We have focused on correcting all grammatical errors, improving sentence structure, and refining the phrasing throughout the document to enhance readability. We are confident that these extensive revisions have significantly improved the clarity of the manuscript. We hope you will find the current version much easier to read and understand.

Reviewer #3 (Recommendations for the authors):

(1) However, I think the abstract part of the article is too detailed and should be more concise and shortened. It is not necessary to show detailed values but to summarize the results.

Thank you for this valuable suggestion. We agree that the previous version of the abstract was overly detailed and that a more concise summary would be more effective for the reader. Following your advice, we have substantially revised the abstract. We have removed the specific numerical values (such as detailed statistics) and have instead focused on summarizing the key findings and their broader implications (Page 3, lines 54-60, 64-66, 70-72). The revised abstract is now shorter and provides a clearer, high-level overview of our study's background, methods, main results, and conclusions. We believe these changes have significantly improved its readability and impact. We hope you will find the current version more appropriate.

(2) Figure 4, the color in the legend and plot are not the same, and should be revised.

Thank you for your careful attention to detail and for pointing out the color inconsistency in Figure 4. We apologize for this oversight. We have now corrected the figure as you suggested, ensuring that the colors in the legend perfectly match those in the plot. The revised Figure 4 has been updated in the manuscript. We appreciate your help in improving the quality of our figures.

(3) Please pay attention to the article format, such as the consistency of fonts and punctuation marks. (For example, Lines 75 and Line 230).

Thank you for your meticulous review and for pointing out the inconsistencies in our manuscript's formatting. We sincerely apologize for these oversights and any inconvenience they may have caused. Following your feedback, we have carefully corrected the specific issues you highlighted. Furthermore, we have conducted a thorough proofread of the entire manuscript to ensure consistency in all fonts, punctuation marks, and overall adherence to the journal's formatting guidelines. We appreciate your help in improving the presentation and professionalism of our paper.

Author response:

(1) General Statements

We thank the Reviewers for a fair review of our work and helpful suggestions. We have significantly revised the manuscript in response to these suggestions. We provide a point-by-point response to the Reviewers below but wanted to highlight in our response a recurring concern related to the strong cell cycle arrest observed upon the acute FAM53C knock-down being different than the limited phenotypes in other contexts, including the knockout mice and DepMap data.

First, we now show that we can recapitulate the strong G1 arrest resulting from the FAM53C knock-down using two independent siRNAs in RPE-1 cells, supporting the specificity of the effects.

Second, the G1 arrest that results from the FAM53C knock-down is also observed in cells with inactive p53, suggesting it is not due to a non-specific stress response due to “toxic” siRNAs. In addition, the arrest is dependent on RB, which fits with the genetic and biochemical data placing FAM53C upstream of RB, further supporting a specific phenotype.

Third, we have performed experiments in other human cells, including cancer cell lines. As would be expected for cancer cells, the G1 arrest is less pronounced but is still significant, indicating that the G1 arrest is not unique to RPE-1 cells.

Fourth, it is not unexpected that compensatory mechanisms would be activated upon loss of FAM53C during development or in cancer – which may explain the lack of phenotypes in vivo or upon long-term knockout. This has been true for many cell cycle regulators, either because of compensation by other family members that have overlapping functions, or by a larger scale rewiring of signaling pathways. 

(2) Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity): 

Summary: 

Taylar Hammond and colleagues identified new regulators of the G1/S transition of the cell cycle.

They did so by screening public available data from the Cancer Dependency Map, and identified FAM53C as a positive regulator of the G1/S transition. Using biochemical assays they then show that FAM53 interacts with the DYRK1A kinase to inhibit its function. DYRK1A in its is known to induce degradation of cyclin D, leading the authors to propose a model in which DYRK1Adependent cyclin D degradation is inhibited by FAM53C to permit S-phase entry. Finally the authors assess the effect of FAM53C deletion in a cortical organoid model, and in Fam53c knockout mice. Whereas proliferation of the organoids is indeed inhibited, mice show virtually no phenotype.  

Major comments: 

The authors show convincing evidence that FAM53C loss can reduce S-phase entry in cell cultures, and that it can bind to DYRK1A. However, FAM53 has multiple other binding partners and I am not entirely convinced that negative regulation of DYRK1A is the predominant mechanism to explain its effects on S-phase entry. Some of the claims that are made based on the biochemical assays, and on the physiological effects of FAM53C are overstated. In addition, some choices made methodology and data representation need further attention. 

(1) The authors do note that P21 levels increase upon FAM53C. They show convincing evidence that this is not a P53-dependent response. But the claim that " p21 upregulation alone cannot explain the G1 arrest in FAM53C-deficient cells (line 138-139) is misleading. A p53-independent p21 response could still be highly relevant. The authors could test if FAM53C knockdown inhibits proliferation after p21 knockdown or p21 deletion in RPE1 cells. 

The Reviewer raises a great point. Our initial statement needed to be clarified and also need more experimental support. We have performed experiments where we knocked down FAM53C and p21 individually, as well as in combination, in RPE-1 cells. These experiment show that p21 knock-down is not sufficient to negate the cell cycle arrest resulting from the FAM53C knockdown in RPE-1 cells (Figure 4B,C and Figure S4C,D).

We now extended these experiments to conditions where we inhibited DYRK1A, and we also compared these data to experiments in p53-null RPE-1 cells. Altogether, these experiments point to activation of p53 downstream of DYRK1A activation upon FAM53C knock-down, and indicate that p21 is not the only critical p53 target in the cell cycle arrest observed in FAM53C knock-down cells (Figure 4 and Figure S4).

(2) The authors do not convincingly show that FAM53C acts as a DYRK1A inhibitor in cells. Figures 4B+C and S4B+C show extremely faint P-CycD1 bands, and tiny differences in ratios. The P values are hovering around the 0.05, so n=3 is clearly underpowered here. Total CycD1 levels also correlate with FAM53C levels, which seems to affect the ratios more than the tiny pCycD1 bands. Why is there still a pCycD1 band visible in 4B in the GFP + BTZ + DYRK1Ai condition? And if I look at the data points I honestly don't understand how the authors can conclude from S4C that knockdown of siFAM53C increases (DYRK1A dependent) increases in pCycD1 (relative to total CycD1). In figure 5C, no blot scans are even shown, and again the differences look tiny. So the authors should either find a way to make these assays more robust, or alter their claims appropriately. 

We appreciate these comments from the Reviewer and have significantly revised the manuscript to address them.

The analysis of Cyclin D phosphorylation and stability are complicated by the upregulation of p21 upon FAM53C knock-down, in particular because p21 can be part of Cyclin D complexes, which may affect its protein levels in cells (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). Instead of focusing on Cyclin D levels and stability, we refocused the manuscript on RB and p53 downstream of FAM53C loss.

We removed previous panel 4B from the revised manuscript. For panels 4E and S4B (now panels S3J and S3K)), we used a true “immunoassay” (as indicated in the legend – not an immunoblot), which is much more quantitative and avoids error-prone steps in standard immunoblots (“Western blots”). Briefly, this system was developed by ProteinSimple. It uses capillary transfer of proteins and ELISA-like quantification with up to 6 logs of dynamic range (see their web site https://www.proteinsimple.com/wes.html). The “bands” we show are just a representation of the luminescence signals in capillaries. We made sure to further clarify the figure legends in the revised manuscript.

The representative Western blot images for 5C-D (now 5F-G) in the original submission are shown in Figure 5E, we apologize if this was not clear. The differences are small, which we acknowledge in the revised manuscript. Note that several factors can affect Cyclin D levels in cells, including the growth rate and the stage of the cell cycle. Our FACS analysis shows that normal organoids have ~63% of cells in G1 and ~13% in S phase; the overall lower proportion of S-phase cells in organoids may make the immunoblot difference appear smaller, with fewer cycling cells resulting in decreased Cyclin D phosphorylation.

Nevertheless, the Reviewer brings up a good point and comments from this Reviewer and the others made us re-think how to best interpret our results. As discussed above, we re-read carefully the Meyer paper and think that FAM53C’s role and DYRK1A activity in cells may be understood when considering levels of both CycD and p21 at the same time in a continuum. While our genetic and biochemical data support a role for FAM53C in DYRK1A inhibition, it is likely that the regulation of cell cycle progression by FAM53C is not exclusively due to this inhibition. As discussed above and below, we noted an upregulation of p21 upon FAM53C knock-down, and activation of p53 and its targets likely contributes significantly to the phenotypes observed. We added new experiments to support this more complex model (Figure 4 and Figure S4, with new model in S4L).

(3) The experiments to test if DYRK1A inhibition could rescue the G1 arrest observed upon FAM53C knockdown are not entirely convincing either. It would be much more convincing if they also perform cell counting experiments as they have done in Figures 1F and 1G, to complement the flow cytometry assays. I suggest that the authors do these cell counting experiments in RPE1 +/- P53 cells as well as HCT116 cells. In addition, did the authors test if P21 is induced by DYRK1Ai in HCT116 cells? 

We repeated the experiments with the DYRK1A inhibitor and counted the cells. In p53-null RPE1 cells, we found that cell numbers do not increase in these conditions where we had observed a cell cycle re-entry (Fig. 4E), which was accompanied by apoptotic cell death (Fig. S4I). Thus, cells re-enter the cell cycle but die as they progress through S-phase and G2/M. We note that inhibition of DYRK1A has been shown to decrease expression of G2/M regulators (PMID: 38839871), which may contribute to the inability of cells treated to DYRK1Ai to divide. Because our data in RPE-1 cells showed that p21 knock-down was not sufficient to allow the FAM53C knock-down cells to re-enter the cell cycle, we did not further analyze p21 in HCT-116 cells.

(4) The data in Figure 5C and 5D are identical, although they are supposed to represent either pCycD1 ratios or p21 levels. This is a problem because at least one of the two cannot be true. Please provide the proper data and show (representative) images of both data types.

We apologize for these duplicated panels in the original submission. We now replaced the wrong panel with the correct data (Fig. 5F,G). 

(5) Line 246: "Fam53c knockout mice display developmental and behavioral defects." I don't agree with this claim. The mutant mice are born at almost the expected Mendelian ratios, the body weight development is not consistently altered. But more importantly, no differences in adult survival or microscopic pathology were seen. The authors put strong emphasis on the IMPC behavioral analysis, but they should be more cautious. The IMPC mouse cohorts are tested for many other phenotypes related to behavior and neurological symptoms and apparently none of these other traits were changed in the IMPC Famc53c-/- cohort. Thus, the decreased exploration in a new environment could very well be a chance finding. The authors need to take away claims about developmental and behavioral defects from the abstract, results and discussion sections; the data are just too weak to justify this. 

We agree with the Reviewer that, although we observed significant p-values, this original statement may not be appropriate in the biological sense. We made sure in the revised manuscript to carefully present these data.

Minor comments: 

(6) Can the authors provide a rationale for each of the proteins they chose to generate the list of the 38 proteins in the DepMap analysis? I looked at the list and it seems to me that they do not all have described functions in the G1/S transition. The analysis may thus be biased. 

To address this point, we updated Table S1 (2nd tab) to provide a better rationale for the 38 factors chosen. Our focus was on the canonical RB pathway and we included RB binding proteins whose function had suggested they may also be playing a role in the G1/S transition. We do agree that there is some bias in this selection (e.g., there are more RB binding factors described) but we hope the Reviewer will agree with us that this list and the subsequent analysis identified expected factors, including FAM53C. Future studies using this approach and others will certainly identify new regulators of cell cycle progression.

(7) Figure 1B is confusing to me. Are these just some (arbitrarily) chosen examples? Consider leaving this heatmap out altogether, of explain in more detail. 

We agree with the Reviewer that this panel was not necessarily useful and possibly in the wrong place, and we removed it from the manuscript. We replaced it with a cartoon of top hits in the screen.

(8) The y-axes in Figures 2C, 2D, 2E, and 4D are misleading because they do not start at 0. Please let the axis start at 0, or make axis breaks. 

We re-graphed these panels.

(9) Line 229: " Consequences ... brain development." This subheader is misleading, because the in vitro cortical organoid system is a rather simplistic model for brain development, and far away from physiological brain development. Please alter the header. 

We changed the header to “Consequences of FAM53C inactivation in human cortical organoids in culture”.

(10) Figure S5F: the gating strategy is not clear to me. In particular, how do the authors know the difference between subG1 and G1 DAPI signals? Do they interpret the subG1 as apoptotic cells? If yes, why are there so many? Are the culturing or harvesting conditions of these organoids suboptimal? Perhaps the authors could consider doing IF stainings on EdU or BrdU on paraffin sections of organoids to obtain cleaner data?

Thank you for your feedback. The subG1 population in the original Figure S5F represents cells that died during the dissociation step of the organoids for FACS analysis. To address this point, we performed live & dead staining to exclude dead cells and provide clearer data. We refined gating strategy for better clarity in the new S5F panel.

(11) Figure S6A; the labeling seems incorrect. I would think that red is heterozygous here, and grey mutant. 

We fixed this mistake, thank you. 

Reviewer #1 (Significance): 

The finding that the poorly studied gene FAM53C controls the G1/S transition in cell lines is novel and interesting for the cell cycle field. However, the lack of phenotypes in Famc53-/- mice makes this finding less interesting for a broader audience. Furthermore, the mechanisms are incompletely dissected. The importance of a p53-indepent induction of p21 is not ruled out. And while the direct inhibitory interaction between FAM53C and DYRK1A is convincing (and also reported by others; PMID: 37802655), the authors do not (yet) convincingly show that DYRK1A inhibition can rescue a cell proliferation defect in FAM53C-deficient cells. 

Altogether, this study can be of interest to basic researchers in the cell cycle field. 

I am a cell biologist studying cell cycle fate decisions, and adaptation of cancer cells & stem cells to (drug-induced) stress. My technical expertise aligns well with the work presented throughout this paper, although I am not familiar with biolayer interferometry. 

Reviewer #2 (Evidence, reproducibility and clarity): 

Summary 

In this study Hammond et al. investigated the role of Dual-specificity Tyrosine Phosphorylation regulated Kinase 1A (DYRK1) in G1/S transition. By exploiting Dependency Map portal, they identified a previously unexplored protein FAM53C as potential regulator of G1/S transition. Using RNAi, they confirmed that depletion of FAM53C suppressed proliferation of human RPE1 cells and that this phenotype was dependent on the presence protein RB. In addition, they noted increased level of CDKN1A transcript and p21 protein that could explain G1 arrest of FAM53Cdepleted cells but surprisingly, they did not observe activation of other p53 target genes. Proteomic analysis identified DYRK1 as one of the main interactors of FAM53C and the interaction was confirmed in vitro. Further, they showed that purified FAM53C blocked the ability of DYRK1 to phosphorylate cyclin D in vitro although the activity of DYRK1 was likely not inhibited (judging from the modification of FAM53C itself). Instead, it seems more likely that FAM53C competes with cyclin D in this assay. Authors claim that the G1 arrest caused by depletion of FAM53C was rescued by inhibition of DYRK1 but this was true only in cells lacking functional p53. This is quite confusing as DYRK1 inhibition reduced the fraction of G1 cells in p53 wild type cells as well as in p53 knock-outs, suggesting that FAM53C may not be required for regulation of DYRK1 function. Instead of focusing on the impact of FAM53C on cell cycle progression, authors moved towards investigating its potential (and perhaps more complex) roles in differentiation of IPSCs into cortical organoids and in mice. They observed a lower level of proliferating cells in the organoids but if that reflects an increased activity of DYRK1 or if it is just an off target effect of the genetic manipulation remains unclear. Even less clear is the phenotype in FAM53C knock-out mice. Authors did not observe any significant changes in survival nor in organ development but they noted some behavioral differences. Weather and how these are connected to the rate of cellular proliferation was not explored. In the summary, the study identified previously unknown role of FAM53C in proliferation but failed to explain the mechanism and its physiological relevance at the level of tissues and organism. Although some of the data might be of interest, in current form the data is too preliminary to justify publication.

Major points 

(1) Whole study is based on one siRNA to Fam53C and its specificity was not validated. Level of the knock down was shown only in the first figure and not in the other experiments. The observed phenotypes in the cell cycle progression may be affected by variable knock-down efficiency and/or potential off target effects. 

We thank the Reviewer for raising this important point. First, we need to clarify that our experiments were performed with a pool of siRNAs (not one siRNA). Second, commercial antibodies against FAM53C are not of the best quality and it has been challenging to detect FAM53C using these antibodies in our hands – the results are often variable. In addition, to better address the Reviewer’s point and control for the phenotypes we have observed, we performed two additional series of experiments: first, we have confirmed G1 arrest in RPE-1 cells with individual siRNAs, providing more confidence for the specificity of this arrest (Fig. S1B); second, we have new data indicating that other cell lines arrest in G1 upon FAM53C knock-down (Fig. S1E,F and Fig. 4F).

(2) Experiments focusing on the cell cycle progression were done in a single cell line RPE1 that showed a strong sensitivity to FAM53C depletion. In contrast, phenotypes in IPSCs and in mice were only mild suggesting that there might be large differences across various cell types in the expression and function of FAM53C. Therefore, it is important to reproduce the observations in other cell types. 

As mentioned above, we have new data indicating that other cell lines arrest in G1 upon FAM53C knock-down (three cancer cell lines) (Fig. S1E,F and Fig. 4F).

(3) Authors state that FAM53C is a direct inhibitor of DYRK1A kinase activity (Line 203), however this model is not supported by the data in Fig 4A. FAM53C seems to be a good substrate of DYRK1 even at high concentrations when phosphorylations of cyclin D is reduced. It rather suggests that DYRK1 is not inhibited by FAM53C but perhaps FAM53C competes with cyclin D. Further, authors should address if the phosphorylation of cyclin D is responsible for the observed cell cycle phenotype. Is this Cyclin D-Thr286 phosphorylation, or are there other sites involved? 

We revised the text of the manuscript to include the possibility that FAM53C could act as a competitive substrate and/or an inhibitor.

We removed most of the Cyclin D phosphorylation/stability data from the revised manuscript. As the Reviewers pointed out, some of these data were statistically significant but the biological effects were small. As discussed above in our response to Reviewer #1, the analysis of Cyclin D phosphorylation and stability are complicated by the upregulation of p21 upon FAM53C knockdown, in particular because p21 can be part of Cyclin D complexes, which may affect its protein levels in cells (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). Instead of focusing on Cyclin D levels and stability, we refocused the manuscript on RB and p53 downstream of FAM53C loss.

We note, however, that we used specific Thr286 phospho-antibodies, which have been used extensively in the field. Our data in Figure 1 with palbociclib place FAM53C upstream of Cyclin D/CDK4,6. We performed Cyclin D overexpression experiments but RPE-1 cells did not tolerate high expression of Cyclin D1 (T286A mutant) and we have not been able to conduct more ‘genetic’ studies. 

(4) At many places, information on statistical tests is missing and SDs are not shown in the plots. For instance, what statistics was used in Fig 4C? Impact of FAM53C on cyclin D phosphorylation does not seem to be significant. In the same experiment, does DYRK1 inhibitor prevent modification of cyclin D? 

As discussed above, we removed some of these data and re-focused the manuscript on p53-p21 as a second pathway activated by loss of FAM53C.

(5) Validation of SM13797 compound in terms of specificity to DYRK1 was not performed. 

This is an important point. We had cited an abstract from the company (Biosplice) but we agree that providing data is critical. We have now revised the manuscript with a new analysis of the compound’s specificity using kinase assays. These data are shown in Fig. S3F-H.

(6) A fraction of cells in G1 is a very easy readout but it does not measure progression through the G1 phase. Extension of the S phase or G2 delay would indirectly also result in reduction of the G1 fraction. Instead, authors could measure the dynamics of entry to S phase in cells released from a G1 block or from mitotic shake off. 

The Reviewer made a good point. As discussed in our response to Reviewer #1, with p53-null RPE-1 cells, we found that cell numbers do not increase in these conditions where we had observed a cell cycle re-entry (Fig. 4E), which was accompanied by apoptotic cell death (Fig. S4I). Thus, cells re-enter the cell cycle but die as they progress through S-phase and G2/M. We note that inhibition of DYRK1A has been shown to decrease expression of G2/M regulators (PMID: 38839871), which may contribute to the inability of cells treated to DYRK1Ai to divide.

Because our data in RPE-1 cells showed that p21 knock-down was not sufficient to allow the FAM53C knock-down cells to re-enter the cell cycle, we did not further analyze p21 in HCT-116 cells. These data indicate that G1 entry by flow cytometry will not always translate into proliferation.

Other points:

(7) Fig. 2C, 2D, 2E graphs should begin with 0 

We remade these graphs.

(8) Fig. 5D shows that the difference in p21 levels is not significant in FAM53C-KO cells but difference is mentioned in the text. 

We replaced the panel by the correct panel; we apologize for this error.

(9) Fig. 6D comparison of datasets of extremely different sizes does not seem to be appropriate

We agree and revised the text. We hope that the Reviewer will agree with us that it is worth showing these data, which are clearly preliminary but provide evidence of a possible role for FAM53C in the brain.

(10) Could there be alternative splicing in mice generating a partially functional protein without exon 4? Did authors confirm that the animal model does not express FAM53C? 

We performed RNA sequencing of mouse embryonic fibroblasts derived from control and mutant mice. We clearly identified fewer reads in exon 4 in the knockout cells, and no other obvious change in the transcript (data not shown). However, immunoblot with mouse cells for FAM53C never worked well in our hands. We made sure to add this caveat to the revised manuscript.

Reviewer #2 (Significance): 

Main problem of this study is that the advanced experimental models in IPSCs and mice did not confirm the observations in the cell lines and thus the whole manuscript does not hold together. Although I acknowledge the effort the authors invested in these experiments, the data do not contribute to the main conclusion of the paper that FAM53C/DYRK1 regulates G1/S transition. 

Reviewer #3 (Evidence, reproducibility and clarity: 

This paper identifies FAM53C as a novel regulator of cell cycle progression, particularly at the G1/S transition, by inhibiting DYRK1A. Using data from the Cancer Dependency Map, the authors suggest that FAM53C acts upstream of the Cyclin D-CDK4/6-RB axis by inhibiting DYRK1A.  Specifically, their experiments suggest that FAM53C Knockdown induces G1 arrest in cells, reducing proliferation without triggering apoptosis. DYRK1A Inhibition rescues G1 arrest in P53KO cells, suggesting FAM53C normally suppresses DYRK1A activity. Mass Spectrometry and biochemical assays confirm that FAM53C directly interacts with and inhibits DYRK1A. FAM53C Knockout in Human Cortical Organoids and Mice leads to cell cycle defects, growth impairments, and behavioral changes, reinforcing its biological importance. 

Strength of the paper: 

The study introduces a novel cell cycle control signalling module upstream of CDK4/6 in G1/S regulation which could have significant impact. The identification of FAM53C using a depmap correlation analysis is a nice example of the power of this dataset. The experiments are carried out mostly in a convincing manner and support the conclusions of the manuscript. 

Critique: 

(1) The experiments rely heavily on siRNA transfections without the appropriate controls. There are so many cases of off-target effects of siRNA in the literature, and specifically for a strong phenotype on S-phase as described here, I would expect to see solid results by additional experiments. This is especially important since the ko mice do not show any significant developmental cell cycle phenotypes. Moreover, FAM53C does not show a strong fitness effect in the depmap dataset, suggesting that it is largely non-essential in most cancer cell lines. For this paper to reach publication in a high-standard journal, I would expect that the authors show a rescue of the S-phase phenotype using an siRNA-resistant cDNA, and show similar S-phase defects using an acute knock out approach with lentiviral gRNA/Cas9 delivery. 

We thank the Reviewer for this comment. Please refer to the initial response to the three Reviewers, where we discuss our use of single siRNAs and our results in multiple cell lines. Briefly, we can recapitulate the G1 arrest upon FAM53C knock-down using two independent siRNAs in RPE-1 cells. We also observe the same G1 arrest in p53 knockout cells, suggesting it is not due to a non-specific stress response. In addition, the arrest is dependent on RB, which fits with the genetic and biochemical data placing FAM53C upstream of RB, further supporting a specific phenotype. Human cancer cell lines also arrest in G1 upon FAM53C knock-down, not just RPE-1 cells. Finally, we hope the Reviewer will agree with us that compensatory mechanisms are very common in the cell cycle – which may explain the lack of phenotypes in vivo or upon long-term knockout of FAM53C.

(2) The S-phase phenotype following FAM53C should be demonstrated in a larger variety of TP53WT and mutant cell lines. Given that this paper introduces a new G1/S control element, I think this is important for credibility. Ideally, this should be done with acute gRNA/Cas9 gene deletion using a lentiviral delivery system; but if the siRNA rescue experiments work and validate an on-target effect, siRNA would be an appropriate alternative. 

We now show data with three cancer cell lines (U2OS, A549, and HCT-116 – Fig. S1E,F and Fig. 4F), in addition to our results in RPE-1 cells and in human cortical organoids. We note that the knock-down experiments are complemented by overexpression data (Fig. 1G-I), by genetic data (our original DepMap screen), and our biochemical data (showing direct binding of FAM53C to DYRK1A).

(3) The western blot images shown in the MS appear heavily over-processed and saturated (See for example S4B, 4A, B, and E). Perhaps the authors should provide the original un-processed data of the entire gels? 

For several of our panels (e.g., 4E and S4B, now panels S3J and S3K)), we used a true “immunoassay” (as indicated in the legend – not an immunoblot), which is much more quantitative and avoids error-prone steps in standard immunoblots (“Western blots”). Briefly, this system was developed by ProteinSimple. It uses capillary transfer of proteins and ELISA-like quantification with up to 6 logs of dynamic range (see their web site https://www.proteinsimple.com/wes.html). The “bands” we show are just a representation of the luminescence signals in capillaries. We made sure to further clarify the figure legends in the revised manuscript.

Data in 4A are also not a western blot but a radiograph.

For immunoblots, we will provide all the source data with uncropped blots with the final submission.

(4) A critical experiment for the proposed mechanism is the rescue of the FAM53C S-phase reduction using DYRK1A inhibition shown in Figure 4. The legend here states that the data were extracted from BrdU incorporation assays, but in Figure S4D only the PI histograms are shown, and the S-phase population is not quantified. The authors should show the BrdU scatterplot and quantify the phenotype using the S-phase population in these plots. G1 measurements from PI histograms are not precise enough to allow for conclusions. Also, why are the intensities of the PI peaks so variable in these plots? Compare, for example, the HCT116 upper and lower panels where the siRNA appears to have caused an increase in ploidy. 

We apologize for the confusion and we fixed these errors, for most of the analyses, we used PI to measure G1 and S-phase entry. We added relevant flow cytometry plots to supplemental figures (Fig. S1G, H, I, as well as Fig. S4E and S4K, and Fig. S5F).

(5) There's an apparent contradiction in how RB deletion rescues the G1 arrest (Figure 2) while p21 seems to maintain the arrest even when DYRK1A is inhibited. Is p21 not induced when FAM53C is depleted in RB ko cells? This should be measured and discussed. 

This comment and comments from the two other Reviewers made us reconsider our model. We re-read carefully the Meyer paper and think that DYRK1A activity may be understood when considering levels of both CycD and p21 at the same time in a continuum (as was nicely showed in a previous study from the lab of Tobias Meyer – Chen et al., Mol Cell, 2013). While our genetic and biochemical data support a role for FAM53C in DYRK1A inhibition, it is obvious that the regulation of cell cycle progression by FAM53C is not exclusively due to this inhibition. As discussed above and below, we noted an upregulation of p21 upon FAM53C knock-down, and activation of p53 and its targets likely contributes significantly to the phenotypes observed. We added new experiments to support this more complex model (Figure 4 and Figure S4, with new model in S4L).

Reviewer #3 (Significance): 

In conclusion, I believe that this MS could potentially be important for the cell cycle field and also provide a new target pathway that could be relevant for cancer therapy. However, the paper has quite a few gaps and inconsistencies that need to be addressed with further experiments. My main worry is that the acute depletion phenotypes appear so strong, while the gene is nonessential in mice and shows only a minor fitness effect in the depmap screens. More convincing controls are necessary to rule out experimental artefacts that misguide the interpretation of the results.

We appreciate this comment and hope that the Reviewer will agree it is still important to share our data with the field, even if the phenotypes in mice are modest.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment:

This valuable study examines how mammals descend effectively and securely along vertical substrates. The conclusions from comparative analyses based on behavioral data and morphological measurements collected from 21 species across a wide range of taxa are convincing, making the work of interest to all biologists studying animal locomotion.

We would like to greatly thank the two reviewers for their time in reviewing this work, and for their valuable comments and suggestions that will help to improve this manuscript.

Overall, we agree with the weaknesses raised, which are mainly areas for consideration in future studies: to study more species, and in a natural habitat context.

We will nevertheless add a few modifications to improve the manuscript, notably by making certain figures more readable, and adding definitions and bibliography in the main text concerning gait characteristics.

We also provide brief comments on each point of weakness raised by the reviewers below, in blue.

Reviewer #1 (Public review):

Summary:

This unique study reports original and extensive behavioral data collected by the authors on 21 living mammal taxa in zoo conditions (primates, tree shrew, rodents, carnivorans, and marsupials) on how descent along a vertical substrate can be done effectively and securely using gait variables. Ten morphological variables reflecting head size and limb proportions are examined in relationship to vertical descent strategies and then applied to reconstruct modes of vertical descent in fossil mammals.

Strengths:

This is a broad and data-rich comparative study, which requires a good understanding of the mammal groups being compared and how they are interrelated, the kinematic variables that underlie the locomotion used by the animals during vertical descent, and the morphological variables that are associated with vertical descent styles. Thankfully, the study presents data in a cogent way with clear hypotheses at the beginning, followed by results and a discussion that addresses each of those hypotheses using the relevant behavioral and morphological variables, always keeping in mind the relationships of the mammal groups under investigation. As pointed out in the study, there is a clear phylogenetic signal associated with vertical descent style. Strepsirrhine primates much prefer descending tail first, platyrrhine primates descend sideways when given a choice, whereas all other mammals (with the exception of the raccoon) descend head first. Not surprisingly, all mammals descending a vertical substrate do so in a more deliberate way, by reducing speed, and by keeping the limbs in contact for a longer period (i.e., higher duty factors).

Weaknesses:

The different gait patterns used by mammals during vertical descent are a bit more difficult to interpret. It is somewhat paradoxical that asymmetrical gaits such as bounds, half bounds, and gallops are more common during descent since they are associated with higher speeds and lower duty factors. Also, the arguments about the limb support polygons provided by DSDC vs. LSDC gaits apply for horizontal substrates, but perhaps not as much for vertical substrates.

We analyzed gait patterns using methods commonly found in the literature and discussed our results accordingly. However, the study of limbs support polygons was indeed developed specifically for studying locomotion on horizontal supports, and may not be applicable for studying vertical locomotion, which is in fact a type of locomotion shared by all arboreal species. In the future, it would be interesting to consider new methods for analyzing vertical gaits.

The importance of body mass cannot be overemphasized as it affects all aspects of an animal's biology. In this case, larger mammals with larger heads avoid descending head-first. Variation in trunk/tail and limb proportions also covaries with different vertical descent strategies. For example, a lower intermembral index is associated with tail-first descent. That said, the authors are quick to acknowledge that the five lemur species of their sample are driving this correlation. There is a wide range of intermembral indices among primates, and this simple measure of forelimb over hindlimb has vital functional implications for locomotion: primates with relatively long hindlimbs tend to emphasize leaping, primates with more even limb proportions are typically pronograde quadrupeds, and primates with relatively long forelimbs tend to emphasize suspensory locomotion and brachiation. Equally important is the fact that the intermembral index has been shown to increase with body mass in many primate families as a way to keep functional equivalence for (ascending) climbing behavior (see Jungers, 1985). Therefore, the manner in which a primate descends a vertical substrate may just be a by-product of limb proportions that evolved for different locomotor purposes. Clearly, more vertical descent data within a wider array of primate intermembral indices would clarify these relationships. Similarly, vertical descent data for other primate groups with longer tails, such as arboreal cercopithecoids, and particularly atelines with very long and prehensile tails, should provide more insights into the relationship between longer tail length and tail-first descent observed in the five lemurs. The relatively longer hallux of lemurs correlates with tail-first descent, whereas the more evenly grasping autopods of platyrrhines allow for all four limbs to be used for sideways descent. In that context, the pygmy loris offers a striking contrast. Here is a small primate equipped with four pincer-like, highly grasping autopods and a tail reduced to a short stub. Interestingly, this primate is unique within the sample in showing the strongest preference for head-first descent, just like other non-primate mammals. Again, a wider sample of primates should go a long way in clarifying the morphological and behavioral relationships reported in this study.

We agree with this statement. In the future, we plan to study other species, particularly large-bodied ones with varied intermembral indexes.

Reconstruction of the ancient lifestyles, including preferred locomotor behaviors, is a formidable task that requires careful documentation of strong form-function relationships from extant species that can be used as analogs to infer behavior in extinct species. The fossil record offers challenges of its own, as complete and undistorted skulls and postcranial skeletons are rare occurrences. When more complete remains are available, the entire evidence should be considered to reconstruct the adaptive profile of a fossil species rather than a single ("magic") trait.

We completely agree with this, and we would like to emphasize that our intention here was simply to conduct a modest inference test, the purpose of which is to provide food for thought for future studies, and whose results should be considered in light of a comprehensive evolutionary model.

Reviewer #2 (Public review):

Summary:

This paper contains kinematic analyses of a large comparative sample of small to medium-sized arboreal mammals (n = 21 species) traveling on near-vertical arboreal supports of varying diameter. This data is paired with morphological measures from the extant sample to reconstruct potential behaviors in a selection of fossil euarchontaglires. This research is valuable to anyone working in mammal locomotion and primate evolution.

Strengths:

The experimental data collection methods align with best research practices in this field and are presented with enough detail to allow for reproducibility of the study as well as comparison with similar datasets. The four predictions in the introduction are well aligned with the design of the study to allow for hypothesis testing. Behaviors are well described and documented, and Figure 1 does an excellent job in conveying the variety of locomotor behaviors observed in this sample. I think the authors took an interesting and unique angle by considering the influence of encephalization quotient on descent and the experience of forward pitch in animals with very large heads.

Weaknesses:

The authors acknowledge the challenges that are inherent with working with captive animals in enclosures and how that might influence observed behaviors compared to these species' wild counterparts. The number of individuals per species in this sample is low; however, this is consistent with the majority of experimental papers in this area of research because of the difficulties in attaining larger sample sizes.

Yes, that is indeed the main cost/benefit trade-off with this type of study. Working with captive animals allows for large comparative studies, but there is a risk of variations in locomotor behavior among individuals in the natural environment, as well as few individuals per species in the dataset. That is why we plan and encourage colleagues to conduct studies in the natural environment to compare with these results. However, this type of study is very time-consuming and requires focusing on a single species at a time, which limits the comparative aspect.

Figure 2 is difficult to interpret because of the large amount of information it is trying to convey.

We agree that this figure is dense. One possible solution would be to combine species by phylogenetic groups to reduce the amount of information, as we did with Fig. 3 on the dataset relating to gaits. However, we believe that this would be unfortunate in the case of speed and duty factor because we would have to provide the complete figure in SI anyway, as the species-level information is valuable. We therefore prefer to keep this comprehensive figure here and we will enlarge the data points to improve their visibility, and provide the figure with a sufficiently high resolution to allow zooming in on the details.

Reviewer #1 (Recommendations for the authors):

As indicated in the first section above, this is a strong comparative study that addresses important questions, relative to the evolution of arboreal locomotion in primates and close mammal relatives. My recommendations should be taken in the context of improving a manuscript that is already generally acceptable.

(1) The terms symmetrical and asymmetrical gaits should be briefly defined in the main text (not just in the Methods section) by citing work done by Hildebrand and other relevant studies. To that effect, the statement on lines 96-97 about the convergence of symmetrical gaits is unclear. What does "Symmetrical gaits have evolved convergently in rodents, scandentians, carnivorans, and marsupials" mean? Symmetrical gaits such as the walk, run, trot, etc., are pretty the norm in most mammals and were likely found in metatherians and basal eutherians. This needs clarification. On line 239, the term "ambling" is used in the context of related asymmetrical gaits. To be clear, the amble is a type of running gait involving no whole-body aerial phase and is therefore a symmetrical gait (see Schmitt et al., 2006).

We have added a definition of the terms symmetrical and asymmetrical gaits and added references in the introduction such as: “Symmetrical gaits are defined as locomotor patterns in which the footfalls of a girdle (a pair of fore- or hindlimbs) are evenly spaced in time, with the right and left limbs of a pair of limbs being approximately 50% out of phase with each other (Hildebrand, 1966, 1967). Symmetrical gaits can be further divided into two types: diagonal-sequence gaits, in which a hindlimb footfall is followed by that of the contralateral forelimb, and lateral-sequence gaits, in which a hindlimb footfall is followed by that of the ipsilateral forelimb (Hildebrand, 1967; Shapiro and Raichlen, 2005; Cartmill et al., 2007b). In contrast, asymmetrical gaits are characterized by unevenly spaced footfalls within a girdle, with the right and left limbs moving in near synchrony (Hildebrand, 1977).” Now found in lines 87-94.

We corrected the sentence such as “Symmetrical gaits are also common in rodents, scandentians, etc..” Now found in line 107.

Thank you for pointing this out. We indeed did not use the right term to mention related asymmetrical gaits with increased duty factors. We removed the term « ambling » and the associated reference here. Now found in line 256.

(2) Correlations are used in the paper to examine how brain mass scales with body mass. It is correct to assume that a correlation significantly different from 0 is indicative of allometry (in this case, positive). That said, lines are used in Figure S2 that go through the bivariate scatter plot. The vast majority of scaling studies rely on regression techniques to calculate and compare slopes, which are different statistically from correlations. In this case, a slope not significantly different from 1.0 would support the hypothesis of isometry based on geometric similarity (as brain mass and body mass are two volumes). The authors could refer to the work of Bob Martin and the 1985 edited book by Jungers and contributions therein. These studies should also be cited in the paper.

Thank you for recommending us this better suited method. We replaced the correlations with major axis orthogonal regressions, as recommended by Martin and Barbour 1989. We found a positive slope for all species significantly different from 1 (0.36), indicating a negative allometry (we realized we were mistaken about the allometry terminology, initially reporting a “positive allometry” instead of a positive correlation).

We corrected in the manuscript in the Results and Methods sections, and cited Martin and Barbour 1989 such as:

“To ensure that the EQs of the different species studied are comparable and meaningful, we tested the allometry between the brain and body masses in our dataset following [84] and found a significant and positive slope for all species (major axis orthogonal regression on log transformed values: slope = 0.36, r² = 0.92, p = 5.0.10^-12), indicating a negative allometry (r = 0.97, df = 19, p = 2.0.10^-13), and similar allometric coefficients when restricting the analysis to phylogenetic groups (Fig. S2).” Now found in lines 289-298.

- “To control that brain allometry is homogeneous among all phylogenetic groups, to be able to compare EQ between species, we computed major axis orthogonal regressions, following the recommendation of Martin and Barbour [84], between the Log transformed brain and body masses, over all species and by phylogenetic group using the sma package in R (Fig. S2).” Now found in lines 336-338.

We also changed Figure S2 in Supplementary Information accordingly.

(3) Trunk length is used as the denominator for many of the indices used in the study. In this way, trunk length is considered to be a proxy for body size. There should be a demonstration that trunk length scales isometrically with body mass in all of the mammals compared. If not the case, some of the indices may not be directly comparable.

We did not use trunk length as a proxy for body mass, but to compute geometric body proportions in order to test whether intrinsic body proportions could be related to vertical descent behaviors, namely the length of the tail and of the fore- and hindlimbs relative to the animal. We chose those indices to quantify the capability of limbs to act as levers or counterweights to rotate the animals for this specific question of vertical descent behavior. We therefore do not think that body mass allometry with respect to trunk length is relevant to compare these indices across species here. Also, we don’t expect that trunk length (which is a single dimension) would scale isometrically with body mass, which scales more as a volume.

(4) Given the numerous comparisons done in this study, a Bonferroni correction method should be considered to mitigate type I error (accepting a false positive).

We had already corrected all our statistical tests using the Benjamini-Hochberg method to control for false positives; see the SuppTables Excel file for the complete results of the statistical analyses. We chose this method over the Bonferroni correction because the more modern and balanced Benjamini-Hochberg procedure is better suited for analyses involving a large number of hypotheses.

(5) The terms "arm" and "leg" used in the main text and Table 1 are anatomically incorrect. Instead, the terms "forelimb" and hindlimb" should be used as they include the length sum of the stylopod, zeugopod, and autopod.

Indeed, thank you for pointing that out. We have corrected this error within the manuscript as well as in the figures 4 and S3.

(6) On p. 14, the authors make the statement that the postcranial anatomy of Adapis and Notharctus remains undescribed. The authors should consult the work of Dagosto, Covert, Godinot and others.

We did not state that the postcranial remains of Adapis and Notharctus have not been described. However, we were unfortunately unable to find published illustrations of the known postcranial elements that could be reliably used in this study. To avoid any misunderstanding, we removed the sentence such as: “However, we could not find suitable illustrations of the known postcranial elements of these species in the literature that could be reliably incorporated into this study. Thus, we only included their reconstructed body mass and EQ,..”. Now found in lines 393-397.

Reviewer #2 (Recommendations for the authors):

(1) Line 65/69 - Perchalski et al. 2021 is a single-author publication, so no et al. or w/ colleagues.

Indeed. This has been corrected in the manuscript, now found in lines 65 and 70.

(2) Lines 96-98 - Is it appropriate to say that the use of symmetrical gaits are examples of convergent evolution? There's less burden of evidence to state that these are shared behaviors, rather than suggesting they independently evolved across all those groups.

We agree with this and corrected the sentence such as “Symmetrical gaits are also common in rodents, scandentians, etc..” Now found in line 107.

(3) Line 198 - I am confused by how to interpret (-16,36 %) compared to how other numbers are presented in the rest of the paragraph.

To avoid confusion, we rephrased this sentence such as: “In contrast, primates did not significantly reduce their speed compared to ascents when descending sideways or tail-first (Fig. 2A, SuppTables B).”  Now found in lines 207-209.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1(Public review):

Summary:

In this study, the authors aim to understand how Rhino, a chromatin protein essential for small RNA production in fruit flies, is initially recruited to specific regions of the genome. They propose that asymmetric arginine methylation of histones, particularly mediated by the enzyme DART4, plays a key role in defining the first genomic sites of Rhino localization. Using a combination of inducible expression systems, chromatin immunoprecipitation, and genetic knockdowns, the authors identify a new class of Rhinobound loci, termed DART4 clusters, that may represent nascent or transitional piRNA clusters.

Strengths:

One of the main strengths of this work lies in its comprehensive use of genomic data to reveal a correlation between ADMA histones and Rhino enrichment at the border of known piRNA clusters. The use of both cultured cells and ovaries adds robustness to this observation. The knockdown of DART4 supports a role for H3R17me2a in shaping Rhino binding at a subset of genomic regions.

Weaknesses:

However, Rhino binding at, and piRNA production from, canonical piRNA clusters appears largely unaffected by DART4 depletion, and spreading of Rhino from ADMArich boundaries was not directly demonstrated. Therefore, while the correlation is clearly documented, further investigation would be needed to determine the functional requirement of these histone marks in piRNA cluster specification.

The study identify piRNA cluster-like regions called DART4 clusters. While the model proposes that DART4 clusters represent evolutionary precursors of mature piRNA clusters, the functional output of these clusters remains limited. Additional experiments could help clarify whether low-level piRNA production from these loci is sufficient to guide Piwi-dependent silencing.

In summary, the authors present a well-executed study that raises intriguing hypotheses about the early chromatin context of piRNA cluster formation. The work will be of interest to researchers studying genome regulation, small RNA pathways, and the chromatin mechanisms of transposon control. It provides useful resources and new candidate loci for follow-up studies, while also highlighting the need for further functional validation to fully support the proposed model.

We sincerely thank Reviewer #1 for the thoughtful and constructive summary of our work. We appreciate the reviewer’s recognition that our study provides a comprehensive analysis of the relationship between ADMA-histones and Rhino localization, and that it raises intriguing hypotheses about the early chromatin context of piRNA cluster formation.

We fully agree with the reviewer that our data primarily demonstrate correlation between ADMA-histones and Rhino localization, rather than direct causation. In response, we have carefully revised the text throughout the manuscript to avoid overstatements implying causality (details provided below).

We also acknowledge the reviewer’s important point that the functional requirement of ADMA-histones for piRNA clusters specification remains to be further established. We have now added the discussion about our experimental limitations (page 18).

Overall, we have revised the manuscript to present our findings more cautiously and transparently, emphasizing that our data reveal a correlation between ADMA-histone marks and the initial localization of Rhino, rather than proving a direct mechanistic requirement. We thank the reviewer again for highlighting these important distinctions.

Reviewer #2 (Public review):

This study seeks to understand how the Rhino factor knows how to localize to specific transposon loci and to specific piRNA clusters to direct the correct formation of specialized heterochromatin that promotes piRNA biogenesis in the fly germline. In particular, these dual-strand piRNA clusters with names like 42AB, 38C, 80F, and 102F generate the bulk of ovarian piRNAs in the nurse cells of the fly ovary, but the evolutionary significance of these dual-strand piRNA clusters remains mysterious since triple null mutants of these dual-strand piRNA clusters still allows fly ovaries to develop and remain fertile. Nevertheless, mutants of Rhino and its interactors Deadlock, Cutoff, Kipferl and Moonshiner, etc, causes more piRNA loss beyond these dual-strand clusters and exhibit the phenotype of major female infertility, so the impact of proper assembly of Rhino, the RDC, Kipferl etc onto proper piRNA chromatin is an important and interesting biological question that is not fully understood.

This study tries to first test ectopic expression of Rhino via engineering a Dox-inducible Rhino transgene in the OSC line that only expresses the primary Piwi pathway that reflects the natural single pathway expression the follicle cells and is quite distinct from the nurse cell germline piRNA pathway that is promoted by Rhino, Moonshiner, etc. The authors present some compelling evidence that this ectopic Rhino expression in OSCs may reveal how Rhino can initiate de novo binding via ADMA histone marks, a feat that would be much more challenging to demonstrate in the germline where this epigenetic naïve state cannot be modeled since germ cell collapse would likely ensue. In the OSC, the authors have tested the knockdown of four of the 11 known Drosophila PRMTs (DARTs), and comparing to ectopic Rhino foci that they observe in HP1a knockdown (KD), they conclude DART1 and DART4 are the prime factors to study further in looking for disruption of ADMA histone marks. The authors also test KD of DART8 and CG17726 in OSCs, but in the fly, the authors only test Germ Line KD of DART4 only, they do not explain why these other DARTs are not tested in GLKD, the UAS-RNAi resources in Drosophila strain repositories should be very complete and have reagents for these knockdowns to be accessible.

The authors only characterize some particular ADMA marks of H3R17me2a as showing strong decrease after DART4 GLKD, and then they see some small subset of piRNA clusters go down in piRNA production as shown in Figure 6B and Figure 6F and Supplementary Figure 7. This small subset of DART4-dependent piRNA clusters does lose Rhino and Kipferl recruitment, which is an interesting result.

However, the biggest issue with this study is the mystery that the set of the most prominent dual-strand piRNA clusters. 42AB, 38C, 80F, and 102F, are the prime genomic loci subjected to Rhino regulation, and they do not show any change in piRNA production in the GLKD of DART4. The authors bury this surprising negative result in Supplementary Figure 5E, but this is also evident in no decrease (actually an n.s. increase) in Rhino association in Figure 5D. Since these main piRNA clusters involve the RDC, Kipferl, Moonshiner, etc, and it does not change in ADMA status and piRNA loss after DART4 GLKD, this poses a problem with the model in Figure 7C. In this study, there is only a GLKD of DART4 and no GLKD of the other DARTs in fly ovaries.

One way the authors rationalize this peculiar exception is the argument that DART4 is only acting on evolutionarily "young" piRNA clusters like the bx, CG14629, and CG31612, but the lack of any change on the majority of other piRNA clusters in Figure 6F leaves upon the unsatisfying concern that there is much functional redundancy remaining with other DARTs not being tested by GLKD in the fly that would have a bigger impact on the other main dual-strand piRNA clusters being regulated by Rhino and ADMA-histone marks.

Also, the current data does not provide convincing enough support for the model Figure 7C and the paper title of ADMA-histones being the key determinant in the fly ovary for Rhino recognition of the dual-strand piRNA clusters. Although much of this study's data is well constructed and presented, there remains a large gap that no other DARTs were tested in GLKD that would show a big loss of piRNAs from the main dual-strand piRNA clusters of 42AB, 38C, 80F, and 102F, where Rhino has prominent spreading in these regions.

As the manuscript currently stands, I do not think the authors present enough data to conclude that "ADMA-histones [As a Major new histone mark class] does play a crucial role in the initial recognition of dual-strand piRNA cluster regions by Rhino" because the data here mainly just show a small subset of evolutionarily young piRNA clusters have a strong effect from GLKD of DART4. The authors could extensively revise the study to be much more specific in the title and conclusion that they have uncovered this very unique niche of a small subset of DART4-dependent piRNA clusters, but this niche finding may dampen the impact and significance of this study since other major dual-strand piRNA clusters do not change during DART4 GLKD, and the authors do not show data GLKD of any other DARTs. The niche finding of just a small subset of DART-4-dependent piRNA clusters might make another specialized genetics forum a more appropriate venue.

We are deeply grateful to Reviewer #2 for the detailed and insightful review that carefully situates our study in the broader context of Rhino-mediated piRNA cluster regulation. We appreciate the reviewer’s recognition that our inducible Rhino expression system in OSCs provides a valuable model to explore de novo Rhino recruitment under a simplified chromatin environment.

At the same time, we agree that the current data mainly support a role for DART4 in regulating a subset of evolutionarily young piRNA clusters, and do not demonstrate a requirement for ADMA-histones at the major dual-strand piRNA clusters such as 42AB or 38C. We have therefore revised the title and main conclusions to more accurately reflect the scope of our findings.

We agree with the reviewer that functional redundancy among DARTs may explain why major dual-strand piRNA clusters are unaffected by DART4 GLKD. Indeed, we have tried DART1 GLKD in the germline, which shows collapse of Rhino foci in OSCs.For DART1 GLKD, two approaches were possible:

(1) Crossing the BDSC UAS-RNAi line (ID: 36891) with nos-GAL4.

(2) Crossing the VDRC UAS-RNAi line (ID: 110391) with nos-GAL4 and UAS-Dcr2.

The first approach was not feasible because the UAS-RNAi line always arrived as dead on arrival (DOA) and could not be maintained in our laboratory. The second approach did not yield effective and stable knockdown (as follows).

DART8 and CG17726 did not alter Rhino foci in OSC knockdown experiments; therefore, we did not attempt germline knockdown (GLKD) of these DARTs in the ovary.  We agree with the reviewer’s opinion that there are piRNA source loci where Rhino localization depends on DART1, and that simultaneous depletion of multiple DARTs may indeed reveal additional positive results because ADMA-histones such as H3R8me2a may be completely eliminated by the knockdown of multiple DARTs. At the same time, we note that many evolutionarily conserved piRNA clusters show a loss of ADMA accumulation compared with evolutionarily young piRNA clusters, with levels that are comparable to the background input in ChIP-seq reads. Therefore, conserved clusters such as 42AB and 38C may no longer be regulated by ADMA. Even if multiple DARTs function redundantly to regulate ADMA, it may be difficult to disrupt Rhino localization at such conserved piRNA clusters by depletion of DARTs. While disruption of Rhino localization at conserved clusters like 42AB and 38C may be challenging, we cannot exclude the possibility that DART depletion affects Rhino binding at less conserved piRNA clusters, where ADMA modification remains detectable. We added clarifications in the Discussion to acknowledge the potential redundancy with other DARTs and to note that further knockdown experiments in the germline will be necessary to test this model comprehensively (page 18).

We appreciate the reviewer’s critical feedback, which has helped us refine the message and strengthen the interpretative balance of the paper.

Reviewer #1 (Recommendations for the authors):

In multiple places, the link between ADMA histones and Rhino recruitment is presented in terms that imply causality. Please revise these statements to reflect that, in most cases, the evidence supports correlation rather than direct functional necessity. Similarly, statements suggesting that ADMA histones promote Rhino spreading should be revised unless supported by direct evidence.

We sincerely thank the reviewer for the insightful comments. We recognize that these suggestions are crucial for improving the manuscript, and we have revised it accordingly to address the concerns. The specific revisions we made are detailed below.

(1) Page 1, line 14: The original sentence “in establishing the sites” was changed to “may establish the potential sites.”

(2) Page 4, lines 11-12: The original sentence “genomic regions where Rhino binds at the ends and propagates in the areas in a DART4-dependent manner, but not stably anchored” was changed to “genomic regions that have ADMA-histones at their ends and exhibit broad Rhino spreading across their internal regions in a DART4dependent manner”

(3) Page4, lines 12-15: The original sentence “Kipferl is present at the regions but not sufficient to stabilize Rhino-genomic binding after Rhino propagates.” was changed to “In contrast to authentic piRNA clusters, Kipferl was lost together with Rhino upon DART4 depletion in these regions, suggesting that Kipferl by itself is not sufficient to stabilize Rhino binding; rather, their localization depends on DART4.”

(4) Page4, lines17-18: The original sentence “are considered to be primitive clusters” was changed to “might be nascent dual-strand piRNA source loci”.

(5) Page 8, line 7: The original sentence “Involvement of ADMA-histones in the genomic localization of Rhino was implicated.” was changed to “Correlation of ADMA-histones in the genomic localization of Rhino was implicated.”

(6) Page 8, lines 19-21: The original sentence “These results suggest that ADMAhistones, together with H3K9me3, contribute significantly and specifically to the recruitment of Rhino to the ends of dual-strand clusters in OSCs.” was changed to “These results raise the possibility that ADMA-histones, together with H3K9me3, may contribute specifically to the recruitment of Rhino to the ends of dual-strand clusters in OSCs.”

(7) Page 10, lines 11-13: The original sentence “These results suggest that DART1 and DART4 are involved in Rhino recruitment at distinct genomic sites through the decreases in ADMA-histones in each of their KD conditions (H4R3me2a and H3R17me2a, respectively).” was changed to ”These results suggest that DART1 and DART4 could contribute to Rhino recruitment at distinct genomic sites through the decreases in ADMA-histones in each of their KD conditions (H4R3me2a and H3R17me2a, respectively).”

(8) Page 13, line 2: The original sentence “Genomic regions where Rhino spreads in a DART4-dependent manner, but not stably anchored, produce some piRNAs“ was changed to “Genomic regions where Rhino binds broadly in a DART4-dependent manner, but not stably anchored, produce some piRNAs”

(9) Page 13, lines 21-22: The original sentence “These results support the hypothesis that ADMA-histones are involved in the genomic binding of Rhino both before and after Rhino spreading, resulting in stable genome binding.” was changed to “These results raise the possibility that a subset of Rhino localized to genomic regions correlating with ADMA-histones may serve as origins of spreading.”

(10) Page 16, lines 6-8: The original sentence “In this study, we took advantage of cultured OSCs for our analysis and found that chromatin marks (i.e., ADMA-histones) play a crucial role in the loading of Rhino onto the genome.” was changed to “In this study, we took advantage of cultured OSCs for our analysis and found that chromatin marks (i.e., bivalent nucleosomes containing H3K9me3 and ADMA-histones) appear to contribute to the initial loading of Rhino onto the genome.”

(11) Page16, line 12: The original sentence “We propose that the process of piRNA cluster formation begins with the initial loading of Rhino onto bivalent nucleosomes containing H3K9me3 and ADMA-histones (Fig. 7C). In OSCs, the absence of Kipferl and other necessary factors means that Rhino loading into the genome does not proceed to the next step.” was removed.

Major points

(1)  Clarify the limited colocalization between Rhino and H3K9me3 in OSCs. The observation that FLAG-Rhino foci show minimal overlap with H3K9me3 in OSCs appears inconsistent with the proposed model by the authors in the discussion, in which Rhino is initially recruited to bivalent nucleosomes bearing both H3K9me3 and ADMA marks. This discrepancy should be addressed. 

We thank the reviewer’s insightful comments. Indeed, ChIP-seq shows that Rhino partially overlaps with H3K9me3 (Fig. 1F), but immunofluorescence did not reveal any detectable overlap (Fig. 1A). We interpret this discrepancy as arising from the fact that immunofluorescence primarily visualizes H3K9me3 foci that are localized as broad domains in the genome, such as those at centromeres, pericentromeres, or telomeres (named chromocenters), whereas the sharp and interspersed H3K9me3 signals along chromosome arms are difficult to detect by immunofluorescence. We now have these explanations in the revised text (page 6).

(2)  Please indicate whether the FLAG-Rhino used in OSCs has been tested for functionality in vivo-for example, by rescuing Rhino mutant phenotypes. This is particularly relevant given that no spreading is observed with this construct.

We thank the reviewer for raising this important point. We have not directly tested the functionality of FLAG-Rhino construct used in OSCs in living Drosophila fly; i.e., it has not been used to rescue Rhino mutant phenotypes in flies. We acknowledge that FLAGRhino has not previously been expressed in OSCs, and that its localization pattern in OSCs differs from that observed in ovaries, where Rhino is endogenously expressed. However, several lines of evidence suggest that the addition of the N-terminal FLAG tag is unlikely to compromise Rhino function

(1) In previous studies, N-terminally tagged Rhino (e.g., 3xFLAG-V5-Precision-GFPRhino) was expressed in a living Drosophila ovary and was shown to localize properly to piRNA clusters, indicating that the tag does not prevent Rhino from binding its genomic targets (Baumgartner et al., 2022; eLife. Fig. 3 supplement 1G).

(2) In Drosophila S2 cells, FLAG-tagged tandem Rhino chromodomains construct was shown to bind H3K9me3/H3K27me3 bivalent chromatin, demonstrating that the FLAG tag does not impair this fundamental chromatin interaction (Akkouche et al., 2025; Nat Struct Mol Biol. Fig. 4b).

(3) GFP-tagged Rhino has been demonstrated to rescue the transposon derepression phenotype of Rhino mutant flies, further supporting that the addition of tags does not abolish its in vivo function. (Parhad et al., 2017; Dev Cell. Fig.1D).

Therefore, we interpret the partial localization of FLAG-Rhino in OSCs as reflecting the specific chromatin environment and regulatory context of OSCs rather than functional impairment due to the FLAG tag.

(3) Given the low levels of piRNA production and the absence of measurable effects on transposon expression or fertility upon DART4 knockdown, the rationale for classifying these regions as piRNA clusters should be clearly stated. Additional experiments could help clarify whether low-level piRNA production from these loci is sufficient to guide Piwidependent silencing. The authors should also consider and discuss the possibility that some of these differences may reflect background-specific genomic variation rather than DART4-dependent regulation per see.

We thank the reviewer for the insightful comments. As noted, DART4 knockdown did not measurably affect transposon expression or fertility. piRNAs generated from DART4associated clusters associate with Piwi but are insufficient for target repression. Although loss of DART4 largely eliminated piRNAs from these clusters, the cluster-derived transcripts themselves were unchanged. To clarify this point, we now refer to these regions as DART4-dependent piRNA-source loci (DART4 piSLs) in the revised text. We also acknowledge that some observed differences may reflect strain-specific genomic variation and have added this caveat on page 16.

(4)  The authors should describe the genomic context of DART4 clusters in more detail. Specifically, it would be helpful to indicate whether these regions overlap with known transposable elements, gene bodies, or intergenic regions, and to report the typical size range of the clusters. Are any of the piRNAs produced from these clusters predicted to target known transcripts? 

We thank the reviewer’s insightful comments. The overlap of DART4 piSL with transposable elements, gene bodies, and intergenic regions is shown in the right panel of Supplementary Fig. 6E (denoted as “Rhino reduced regions in DART4 GLKD” in the figure). The typical size range of these clusters is presented in Supplementary Fig. 6G. The annotation of piRNA reads derived from these piSL is shown in the right panel of Supplementary Fig. 6F, indicating that most of them appear to target host genes. The specific genes and transposons matched by the piRNAs produced from DART4 piSL are listed in Supplementary Table 8.

(5)  While correlations between Rhino and ADMA histone marks (especially H3R8me2a,H3R17me2a, H4R3me2a) are robust, many ADMA-enriched regions do not recruit Rhino. Please discuss this observation and consider the possible involvement of additional factors.

We thank the reviewer’s insightful comments. As pointed out, not all ADMA-enriched regions recruit Rhino; rather, Rhino is recruited only at sites where ADMAs overlap with H3K9me3. Furthermore, the combination of H3K9me3 and ADMAs alone does not fully account for the specificity of Rhino recruitment, suggesting the involvement of additional co-factors (for example, other ADMA marks such as H3R42me2a, or chromatininteracting proteins). In addition, since histone modifications—including arginine methylation—have the possibility that they are secondary consequences of modifications on other proteins rather than primary regulatory events, it is possible that DART1/4 contribute to Rhino recruitment not only through histone methylation but also via arginine methylation of non-histone chromatin-interacting factors. However, methylation of HP1a does not appear to be involved (Supplementary Fig. 3G). We have added new sentences about these points in the Discussion section (page 18).

(6) The manuscript states that Kipferl is present at DART4 clusters but does not stabilize Rhino binding. Please specify which experimental results support this conclusion and explain.

We apologize for the lack of clarity regarding Kipferl data. Supplementary Fig. 7A and 7B show that Kipferl localizes at major DART4 piSL. This Kipferl localization is lost together with Rhino upon DART4 GLKD, indicating that Rhino localization at DART4 piSL depends on DART4 rather than on Kipferl. From these results, we infer that, unlike at authentic piRNA clusters, Kipferl may not be sufficient to stabilize the association of Rhino with the genome at DART4 piSL. We have added this interpretation on page 14.

Minor points

(1) Figure 1D: Please specify which piRNA clusters are included in the metaplot - all clusters, or only the major producers? 

We thank the reviewer for the question. The metaplot was not generated from a predefined list of “all” piRNA clusters or only the “major producers.” Instead, it was constructed from Rhino ChIP–seq peaks (“Rhino domains”) that are ≥1.5 kb in length.These Rhino domains mainly correspond to the subregions within major dual-strand clusters (e.g., 42AB, 38C) as well as additional clusters such as 80F, 102F, and eyeless, among others. We have provided the full list of domains and their corresponding piRNA clusters (with genomic coordinates) in Supplementary Table 9 and added the additional explanation in Fig. 1d legend.

(2) Supplemental Figure 5E is referred to as 5D in the main text.

We corrected the figure citations on pages 11-12: the reference to Supplementary Fig. 5E has been changed to 5D, and the reference to Supplementary Fig. 5F has been changed to 5E.

(3) Supplemental Figure 7C: The color legend does not match the pie chart, which may confuse readers.

We thank the reviewer for the helpful comment. We are afraid we were not entirely sure what specific aspect of the legend was confusing, but to avoid any possible misunderstanding, we revised Supplemental Fig. 7C so that the color boxes in the legend now exactly match the corresponding colors in the pie chart. We hope this modification improves clarity.

(4) Since the manuscript focuses on the roles of DART1 and DART4, including their expression profiles in OSCs and ovaries would help contextualize the observed phenotypes. Please consider adding this information if available.

We thank the reviewer for the suggestion. We have now included a scatter plot comparing RNA-seq expression in OSCs and ovaries (Supplementary Fig. 3H). In these datasets, DART1 is strongly expressed in both tissues, whereas DART4 shows no detectable reads. Notably, ref. 28 reports strong expression of both DART1 and DART4 in ovaries by western blot and northern blot. In our own qPCR analysis in OSCs, DART4 expression is about 3% of DART1, which, although low, may still be sufficient for functional roles such as modification of H3R17me2a (Fig. 3C, Supplementary Fig. 3F and 3I). We have added these new data and additional explanation in the revised manuscript (page 11).

(5) Several of the genome browser snapshots, particularly scale and genome coordinates, are difficult to read. 

We apologize for the difficulty in reading several of the genome browser snapshots in the original submission. We have re-generated the relevant figures using IGV, which provides clearer visualization of scale and genome coordinates. The previous images have been replaced with the improved versions in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

(1) The authors need to elaborate on what this sentence means, as it is very unclear what they are describing about Rhino residency: "The results show that Rhino in OSCs tends to reside in the genome where Rhino binds locally in the ovary (Fig. 1C)." 

We apologize for the lack of clarity in the original sentence. The text has been revised as follows:

”Rhino expressed in OSCs bound predominantly to genomic sites exhibiting sharp and interspersed Rhino localization patterns in the ovary, while showing little localization within broad Rhino domains, including major piRNA clusters.”

In addition, to clarify the behavior of Rhino at broad domains, we have added the phrase “the terminal regions of broad domains, such as major piRNA clusters” to the subsequent sentence.

(2) The red correlation line is very confusing in Figure 5F. What sort of line does this mean in this scatter plot? 

We apologize for the lack of clarity regarding the red line in Fig. 5F. The red line represents the least-squares linear regression fit to the data points, calculated using the lm() function in R, and was added with abline() to illustrate the correlation between ctrl GLKD and DART4 GLKD values. In the revised figure, we have clarified this in the legend by specifying that it is a regression line.

(3) There is no confirmation of the successful knockdown of the various DARTs in the OSCs.

We thank the reviewer for the comment. The knockdown efficiency of the various DARTs in OSCs was confirmed by RT–qPCR. The data are now shown in Supplementary Fig. 3J. 

(4) What is the purpose of an unnumbered "Method Figure" in the supplementary data file? Why not just give it a number and mention it properly in the text? 

We thank the reviewer for the suggestion. We have now assigned a number to the previously unnumbered "Method Figure" and have included it as Supplementary Fig. 9.

The figure is now properly cited in the Methods section.

(5) For Figure 5A, those fly strain numbers in the labels are better reserved in the Methods, and a more appropriate label is to describe the GAL4 driver and the UAS-RNAi construct by their conventional names.

We thank the reviewer for the suggestion. The labels in Fig. 5A have been updated to use the conventional names of the GAL4 drivers and UAS-RNAi constructs. Specifically, they now read Ctrl GLKD (nos-GAL4 > UAS-emp) and DART4 GLKD (nos-GAL4 > UASDART4). The original fly strain numbers are listed in the Methods section.

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment

This useful study presents the potentially interesting concept that LRRK2 regulates cellular BMP levels and their release via extracellular vesicles, with GCase activity further modulating this process in mutant LRRK2-expressing cells. However, the evidence supporting the conclusions remains incomplete, and certain statistical analyses are inadequate. This work would be of interest to cell biologists working on Parkinson's disease.

Reviewer #1 (Public review):

Summary:

Even though mutations in LRRK2 and GBA1 (which encodes the protein GCase) increase the risk of developing Parkinson's disease (PD), the specific mechanisms driving neurodegeneration remain unclear. Given their known roles in lysosomal function, the authors investigate how LRRK2 and GCase activity influence the exocytosis of the lysosomal lipid BMP via extracellular vesicles (EVs). They use fibroblasts carrying the PDassociated LRRK2-R1441G mutation and pharmacologically modulate LRRK2 and GCase activity.

Strengths:

The authors examine both proteins at endogenous levels, using MEFs instead of cancer cells. The study's scope is potentially interesting and could yield relevant insights into PD disease mechanisms.

Weaknesses:

Many of the authors' conclusions are overstated and not sufficiently supported by the data. Several statistical errors undermine their claims. Pharmacological treatment is very long, leading to potential off-target effects. Additionally, the authors should be more rigorous when using EV markers.

We thank the reviewer for these valuable observations. In the revised manuscript, we have addressed each of these points as follows:

(1) Conclusions and data support – We carefully revised our text throughout the manuscript to ensure that all conclusions are better supported by the presented data. For instance, we now explicitly state that while pharmacological modulation supports the regulatory role of LRRK2 activity in EV-mediated BMP release, we have softened our conclusions concerning the contribution of GCase in this model (see revised Results and Discussion sections).

(2) Statistical analyses – We reanalyzed experiments involving more than two groups and replaced simple t-tests with non-parametric Kruskal-Wallis tests followed by Dunn’s post hoc comparisons. This approach, described in the updated figure legends (e.g., Figure 2D-F and H-J), provides a more rigorous statistical framework that accounts for small sample sizes and variability typical of EV quantifications.

(3) Pharmacological treatment duration – Prolonged MLi-2 treatments have been extensively used in the field without evidence of significant off-target effects. Several studies, including Fell et al. (2015, J Pharmacol Exp Ther 355:397-409), De Wit et al. (2019, Mol Neurobiol 56:5273-5286), Ho et al. (2022, NPJ Parkinson’s Dis 8:115),Tengberg et al. (2024, Neurobiol Dis 202:106728), and Jaimon et al. (2025, Sci Signal 18:eads5761), have applied long-term (24-48 h) MLi-2 treatments at comparable concentrations without detecting toxicity or off-target alterations, including in MEFs (Ho et al., 2022; Dhekne et al., 2018, eLife 7:e40202).  In our study, 48-hour incubations were necessary to sustain full LRRK2 inhibition throughout the extracellular vesicle (EV) collection period. EV biogenesis, BMP biosynthesis, and packaging into EVs are timedependent processes; therefore, extended incubation and collection periods (48 h) were required to allow downstream effects of LRRK2 inhibition on BMP production and release to manifest, and to obtain sufficient EV material for biochemical and lipidomic analyses. This experimental design also reflects our and others’ previous observations in humans and non-human primates, where urinary BMP changes are associated with chronic or subchronic LRRK2 inhibitor treatment (Baptista MAS, Merchant K, et al. Sci Transl Med. 2020, 12:eaav0820; Jennings D, et al. Sci Transl Med. 2022, 14:eabj2658; Maloney MT, et al. Mol Neurodegener. 2025, 20:89). Importantly, under these conditions, we did not observe significant changes in cell viability or morphology, supporting that the treatment was well tolerated.  We have clarified this rationale in the revised Methods section to emphasize that the prolonged incubation reflects the experimental design for EV isolation rather than a requirement for achieving LRRK2 inhibition.

(4) EV markers – We and others have reported enrichment of Flotillin-1 and LAMP proteins in isolated small EV fractions (Kowal et al., 2016; Lu et al., 2018; Mathieu et al., 2021; Ferreira et al., 2022). Moreover, LAMP proteins have been reported to be more enriched in EVs of endolysosomal origin (Mathieu et al., 2021). To further strengthen this point, we performed new experiments using a CD63-pHluorin sensor combined with TIRF microscopy, which allowed real-time visualization of CD63-positive exosome release. These new data (now presented in Figure 7, Panels G-I; Videos 1 and 2) confirm increased CD63-positive EV release in LRRK2 mutant fibroblasts, which was reversed by LRRK2 inhibition with MLi-2. The CD63-positive compartment was also largely BMPpositive (new Figure 7D, F, G), reinforcing our conclusions and providing additional rigor in EV marker validation.

Reviewer #2 (Public review):

Summary:

In this paper, the authors used MEFs expressing the R1441G mutant of leucine-rich repeat kinase 2 (LRRK2), a mutant associated with the early onset of Parkinson's disease. They report that in these cells LAMP2 fluorescence is higher but BMP fluorescence is lower, MVE size is reduced, and that MVEs contain less ILVs. They also report that LAMP2-positive EVs are increased in mutant cells in a process sensitive to LRRK2 kinase inhibition but are further increased by glucocerebrosidase (GCase) inhibition, and that total di-22:6-BMP and total di-18:1-BMP are increased in mutant LRRK2 MEFs compared to WT cells by mass spectrometry. They also report that LRRK2 kinase inhibition partially restores cellular BMP levels, and that GCase inhibition further increases BMP levels, and that in EVs from the LRRK2 mutant, LRRK2 inhibition decreases BMP while GCase inhibition has the opposite effect. Moreover, they report that the BMP increase is not due to increased BMP synthesis, although the authors observe that CLN5 is increased in LRRK2 mutant cells. Finally, they report that GW4869 decreases EV release and exosomal BMP, while bafilomycin A1 increases EV release. They conclude that LRRK2 regulates BMP levels (in cells) and release (via EVs). They also conclude that the process is modulated by GCase in LRRK2 mutant cells, and that these studies may contribute to the use of BMP-positive EVs as a biomarker for Parkinson's disease and associated treatments.

Strengths:

This is an interesting paper, which provides novel insights into the biogenesis of exosomes with exciting biomedical potential. However, I have comments that authors need to address to clarify some aspects of their study.

Weaknesses:

(1) The intensity of LAMP2 staining is increased significantly in cells expressing the R1441G mutant of LRRK2 when compared to WT cells (Figure 1C). Yet mutant cells contain significantly smaller MVEs with fewer ILVs, and the MVE surface area is reduced (Figure 1D-F). This is quite surprising since LAMP2 is a major component of the limiting membrane of late endosomes. Are other proteins of endo-lysosomes (eg, LAMP1, CD63, RAB7) or markers (lysotracker) also decreased (see also below)?

As referenced in our original manuscript, several previous studies have reported endolysosomal morphological and homeostatic defects in cells harboring pathogenic LRRK2 mutations. LAMP2 can be upregulated as part of a lysosomal biogenesis or stress response (e.g., via MiT/TFE transcription factors such as TFEB; Sardiello et al., Science 2009, 325:473-477), whereas ILV biogenesis is primarily controlled by ESCRT- and SMPD3-dependent pathways that are regulated independently of MiT/TFE-driven transcriptional programs. Indeed, Stuffers et al. (Traffic 2009, 10:925-937) demonstrated that depletion of key ESCRT subunits markedly inhibited ILV formation while concomitantly increasing LAMP2 expression, highlighting the mechanistic dissociation between LAMP2 abundance and ILV number. In our study, we observed a similar pattern in R1441G LRRK2 MEFs, in which elevated LAMP2 staining and protein levels occurred despite a reduction in MVE size and ILV number. We interpret this as a compensatory lysosomal biogenesis response.

Our revised manuscript now includes new immunofluorescence data for BMP, LAMP1 and CD63 (New Figure 7, Panels A-F) together with biochemical analysis of CD63 protein levels (New Supplemental Figure 4, Panel B) in human skin fibroblasts derived from healthy donors and LRRK2 G2019S PD patients. Quantitative analysis of these experiments revealed no statistically significant differences in total cellular levels of either LAMP1 or CD63 between groups. However, we observed a consistent decrease in BMP immunostaining intensity (New Figure 7, Panel A and B), in agreement with our findings in mouse fibroblasts. We therefore propose that the elevated LAMP2 expression observed in the engineered MEF clone expressing R1441G may reflect a cell type-specific effect, potentially linked to differential penetrance of LRRK2 signaling on the lysosomal biogenesis response. We have updated the Results and Discussion section of the manuscript to incorporate and clarify these findings.

(2) LRRK2 has been reported to interact with endolysosomal membranes. Does the R1441G mutant bind LAMP2- and/or BMP-positive membranes? 

We agree that LRRK2 has been reported to associate dynamically with endolysosomal membranes, particularly under conditions of endolysosomal stress or damage (Eguchi T, et al. PNAS 2018, 115:E9115-E9124; Bonet-Ponce L, et al. Sci Adv. 2020, 6:eabb2454; Wang X, et al. Elife. 2023, 12:e87255).

Nevertheless, to explore whether LRRK2 associates with BMP-positive endolysosomes, we performed subcellular fractionation followed by biochemical analysis of endolysosomal fractions, since our available LRRK2 antibodies did not provide reliable immunofluorescence signals. These experiments were carried out using human skin fibroblasts derived from both healthy controls and Parkinson’s disease patients carrying the LRRK2-G2019S mutation. In both control and mutant fibroblasts, a pool of LRRK2 was detected in fractions positive for the BMP synthase CLN5 and the endolysosomal marker CD63 (New Supplementary Figure 4, Panel A), supporting the localization of LRRK2 to endolysosomal membranes that are likely BMP-enriched. Our manuscript’s Results and Methods sections have been updated accordingly.

Does the mutant affect endolysosomes?

As referenced in our original manuscript, several studies have reported that pathogenic LRRK2 mutations can lead to endolysosomal defects. Consistent with these reports, we also observed morphological alterations in endolysosomes of cells expressing mutant LRRK2, including reduced MVE size and fewer ILVs, as shown in Figure 1D–F. These observations are in agreement with previously described phenotypes associated with pathogenic LRRK2 variants. Furthermore, in mutant LRRK2 MEFs, and now in humanderived fibroblasts (see new Figure 7, Panel A and B), we observed a decrease in BMP immunostaining signal.

(3) Immunofluorescence data indicate that BMP is decreased in mutant LRRK2expressing cells compared to WT (Figure 1A-B), but mass spec data indicate that di-22:6BMP and di-18:1-BMP are increased (Figure 3). Authors conclude that the BMP pool detected by mass spec in mutant cells is less antibody-accessible than that present in wt cells, or that the anti-BMP antibody is less specific and that it detects other analytes. This is an awkward conclusion, since the IF signal with the antibody is lower (not higher): why would the antibody be less specific? Could it be that the antibody does not see all BMP isoforms equally well? Moreover, the observations that mutant cells contain smaller MVEs (Figure 1D-F) with fewer ILVs are consistent with the IF data and reduced BMP amounts. This needs to be clarified.

As previously reported by us (Lu et al., J Cell Biol 2022;221:e202105060) and others (Berg AL, et al. Cancer Lett. 2023, 557:216090), discrepancies can occur between BMP levels detected by immunofluorescence and those quantified by mass spectrometry. This is because immunostaining reflects the pool of antibody-accessible BMP, whereas lipidomics measures the total cellular content of all BMP molecular species, irrespective of their distribution or accessibility.

We agree that the anti-BMP antibody may not detect all BMP isoforms equally well. Differences in acyl chain composition (such as the degree of saturation or chain length) can alter the stereochemistry of BMP and, consequently, epitope accessibility to antibody binding.

In addition, in a personal communication with Monther Abu-Remaileh (Stanford University), we were informed that the antibody may also cross-react with other lipid species in endolysosomes. Nevertheless, since there is no formal evidence supporting this, we have removed the sentence in the Discussion section stating “Alternatively, the antibody may also detect non-BMP analytes” to avoid any potential misinterpretations. In its place, we have added a short statement noting that “not all BMP isoforms may be detected equally well”.

Mass spectrometry data are only shown for two BMP species (di-22:6, di-18:1). What are the major BMP isoforms in WT cells? The authors should show the complete analysis for all BMP species if they wish to draw quantitative conclusions about the amounts of BMP in wt and mutant cells. Finally, BMP and PG are isobaric lipids. Fragmentation of BMPs or PGs results in characteristic fingerprints, but the presence of each daughter ion is not absolutely specific for either lipid. This should be clarified, e.g., were BMP and PG separated before mass spec analysis? Was PG affected? The authors should also compare the BMP data with mass spec data obtained with a control lipid, e.g., PC.

Regarding BMP isoforms, our targeted UPLC-MS/MS analyses revealed that 2,2′-di-22:6-BMP (sn2/sn2′) and 2,2′-di-18:1-BMP (sn2/sn2′) are the predominant BMP isoforms in MEF cells, consistent with previous reports showing docosahexaenoyl (22:6; DHA) and oleoyl (18:1) BMP as the most abundant isoforms. Across diverse mammalian cells and tissues, BMP typically exhibits a fatty acid composition dominated by oleoyl, with polyunsaturated fatty acids (particularly DHA) also contributing substantially. Enrichment of DHA-containing BMP species has been observed in multiple systems, including rat uterine stromal cells, PC12 cells, THP-1 and RAW macrophages, as well as in rat and human liver. This consistent presence of oleoyl- and docosahexaenoyl-containing BMP species across tissues indicates that these acyl chains are conserved features influencing the lipid’s structural and functional characteristics (Kobayashi et al. J Biol Chem, 2002; Hullin-Matsuda et al. Prostaglandins Leukotriens Essent Fatty Acids, 2009; Thompson et al. Int J Toxicol. 2012; Delton-Vandenbroucke et al. J Lipid Res, 2019).

Nevertheless, we have included a Table (Panel H in updated Supplemental Figure 1) showing other BMP species that were also detected in our lipidomics analysis. Overall, dioleoyl (18:1)- and di-docosahexaenoyl (22:6)-BMP species were the most abundant in MEF cells, whereas di-arachidonoyl (20:4)- and di-linoleoyl (18:2)-BMP isoforms were present at lower levels. Consistently, R1441G LRRK2 MEFs displayed higher levels of dioleoyl- and di-docosahexaenoyl-BMP compared with WT cells, and these elevations were reduced following LRRK2 kinase inhibition with MLi-2. Data from three independent representative experiments are shown, and the manuscript has been revised accordingly to include these results.

Regarding the separation of BMP and PG species, we confirm that BMP and PG were chromatographically resolved prior to MS/MS detection using a validated UPLC-MS/MS method developed by Nextcea, Inc. PG exhibits a substantially longer LC retention time than BMP, ensuring complete baseline separation. This approach (established by Nextcea nearly two decades ago and later validated through a multi-year collaboration with the U.S. FDA to clinically qualify di-22:6-BMP as a biomarker) prevents any ambiguity arising from the isobaric nature of BMP and PG species. No changes in PG levels were detected under any experimental conditions.

Finally, we employed isotope-labeled BMP as an internal standard to ensure robust normalization across samples. These additional details and references cited above have been included in the revised Methods and References sections to further clarify the analytical rigor of our lipidomics workflow.

(4) It is quite surprising that the amounts of labeled BMP continue to increase for up to 24h after a short 25min pulse with heavy BMP precursors (Figure 4B).

In these isotope-labeling experiments, it is important to note (as described in our original manuscript) that two distinct pools of metabolically labeled BMP species were detected: semi-labeled BMP (with only one heavy isotope-labeled fatty acyl chain) and fully-labeled BMP (with both fatty acyl chains labeled). We consider the fully-labeled BMP pool to provide the most reliable readout for BMP turnover, as it showed a rapid decline after a 1h chase (decreasing by more than 50% within 8 h in all conditions), reaching its lowest levels at the end of the 48-h chase period.

The apparent increase in semi-labeled BMP species over time may be explained by continued incorporation of labeled precursors following the initial pulse. Specifically, once existing semi-labeled and fully-labeled BMP molecules are degraded by PLA2G15 (Nyame K, et al. Nature 2025, 642:474-483), the resulting isotope-labeled lysophosphatidylglycerol (LPG) and fatty acids could be recycled and re-enter a new round of BMP biosynthesis, leading to a gradual accumulation of semi-labeled BMP such as di-18:1-BMP. Why would this reasoning not also apply to the fully-labeled species? Once the pulse is completed, newly incorporated non-labeled fatty acyl chains present in the cellular pool can compete with labeled ones during subsequent rounds of lipid remodeling or synthesis. As a result, the probability of generating semi-labeled BMP molecules becomes higher than that of forming fully-labeled species. Consistent with this, our data show an increase in only semi-labeled BMP species (but not in fully-labeled ones) up to 24 hours after the pulse. We have added a clarification regarding this point in the revised manuscript.

(5) It is argued that upregulation of CLN5 may be due to an overall upregulation of lysosomal enzymes, as LAMP2 levels were also increased (Figure 2A, C, E). Again, this is not consistent with the observed decrease in MVE size and number (Figure 1D-F). As mentioned above, other independent markers of endo-lysosomes should be analyzed (eg, LAMP1, CD63, RAB7), and/or other lysosomal enzymes (e.g. cathepsin. D).

Our revised manuscript now includes new immunofluorescence data for BMP, LAMP1 and CD63 (New Figure 7, Panels A-F) together with biochemical analysis of CD63 protein levels (New Supplemental Figure 4, Panel B) in human skin fibroblasts derived from healthy controls and LRRK2 G2019S PD patients. Quantitative analysis of these experiments revealed no statistically significant differences in total cellular levels of either LAMP1 or CD63 between groups. However, our results consistently show increased CLN5 protein levels in both mouse and human fibroblast cell lines harboring pathogenic LRRK2 mutations. Upregulation of CLN5 may reflect a compensatory effect from loss of BMP via EV exocytosis. As discussed above, the elevated LAMP2 signal observed in the engineered MEF clone expressing R1441G could represent a cell type-specific effect, potentially linked to differential penetrance of LRRK2 signaling on the lysosomal biogenesis response. Our Results and Discussion sections have been updated accordingly.

(6) The authors report that the increase in BMP is not due to an increase in BMP synthesis (Figure 4), although they observe a significant increase in CLN5 (Figure 5A) in LRRK2 mutant cells. Some clarification is needed.

In our original manuscript, we proposed that although CLN5 protein levels are increased in R1441G LRRK2 MEFs, the absence of significant changes in BMP synthesis rates (Figure 4B, C) may reflect either limited substrate availability or that CLN5 is already operating near its maximal enzymatic capacity. Our new subcellular fractionation data (new Figure 7, Panel A) further indicate that, despite a relative increase in total CLN5 levels in G2019S LRRK2 human fibroblasts, the amount of CLN5 associated with endolysosomes remains comparable between mutant LRRK2 and control cells. This suggests that a considerable fraction of upregulated CLN5 may not localize to endolysosomes, potentially accumulating in the endoplasmic reticulum due to enhanced translation or impaired trafficking. Unfortunately, the available anti-CLN5 antibody did not yield reliable immunofluorescence signals, preventing us from directly confirming this possibility. Nevertheless, in light of our new data (new Supplemental Figure 4A), we have included a clarification in the revised manuscript discussing this possibility as well.

(7) Authors observe that both LAMP2 and BMP are decreased in EVs by GW4869 and increased by bafilomycin (Figure 6). Given my comments above on Figure 1, it would also be nice to illustrate/quantify the effects of these compounds on cells by immunofluorescence.

We appreciate the reviewer’s suggestion. We have previously published immunofluorescence data showing increased BMP accumulation in endolysosomes following treatment with bafilomycin A1 Lu A, et al. J Cell Biol. 2009, 184:863-879). However, in the present study, our lipidomics analyses revealed a decrease in both di22:6-BMP and di-18:1-BMP species in cells treated with this compound. As discussed above, this apparent discrepancy likely reflects methodological differences between immunofluorescence, which detects only antibody-accessible BMP pools, and lipidomics, which quantifies total cellular BMP content. 

Moreover, in a recent study (Andreu Z, et al. Nanotheranostics 2023, 7:1-21), BMP levels were analyzed by immunofluorescence in cells treated with spiroepoxide, a potent and selective irreversible inhibitor of nSMase (different from GW4869) known to block EV release. Spiroepoxide-treated cells showed decreased BMP immunostaining; a result that, again, does not align with mass spectrometry data revealing increased cellular BMP levels upon GW4869 treatment. Notably, in that study, spiroepoxide was used instead of GW4869 because the intrinsic autofluorescence of GW4869 could potentially interfere with the immunofluorescence BMP signal.

We therefore consider lipidomics measurements to provide a more reliable and quantitative representation of BMP dynamics under these conditions.

Reviewer #1 (Recommendations for the authors):

Major concerns:

(1) 48 h for MLi2 treatment seems too long. LRRK2 kinase activity is inhibited with much shorter incubation times. The longer the incubation, the more likely off-target effects are. The authors should repeat these experiments with 1-2 h of MLi2.

We thank the reviewer for this valuable comment. We acknowledge that MLi-2 is a potent and selective LRRK2 kinase inhibitor that achieves near-complete target engagement within a few hours of treatment. However, prolonged exposure has been widely used in the field without evidence of significant off-target effects. Several studies, including Fell et al. (2015, J Pharmacol Exp Ther 355:397-409), De Wit et al. (2019, Mol Neurobiol 56:5273-5286), Ho et al. (2022, NPJ Parkinson’s Dis 8:115), Tengberg et al. (2024, Neurobiol Dis 202:106728), and Jaimon et al. (2025, Sci Signal 18:eads5761), have employed long-term (24-48 h) MLi-2 treatments at comparable concentrations without detecting toxicity or off-target alterations, including in MEFs (Ho et al., 2022; Dhekne et al., 2018, eLife 7:e40202).

In our study, 48-hour incubations were necessary to sustain full LRRK2 inhibition throughout the extracellular vesicle (EV) collection period. EV biogenesis, BMP biosynthesis, and packaging into EVs are time-dependent processes; therefore, extended incubation and collection periods (48 h) were required to allow downstream effects of LRRK2 inhibition on BMP production and release to manifest, and to obtain sufficient EV material for biochemical and lipidomic analyses. This experimental design also reflects our and others’ previous observations in humans and non-human primates, where urinary BMP changes are associated with chronic or subchronic LRRK2 inhibitor treatment (Baptista MAS, Merchant K, et al. Sci Transl Med. 2020, 12:eaav0820; Jennings D, et al. Sci Transl Med. 2022, 14:eabj2658; Maloney MT, et al. Mol Neurodegener. 2025, 20:89). Importantly, under these conditions, we did not observe significant changes in cell viability or morphology, supporting that the treatment was well tolerated.

We have clarified this rationale in the revised Methods section to emphasize that the prolonged incubation reflects the experimental design for EV isolation rather than a requirement for achieving LRRK2 inhibition.

(2) Is there a reason why the authors don't include CD81, CD63, and Syntenin-1 in their study as an EV marker? Using solely Flotilin-1 does not seem to be enough to justify their claims.

We actually used not only Flotillin-1 but also LAMP2 as EV markers in our study. While both Flotillin-1 and LAMP2 detection on EVs may vary depending on the cell type, we and others have reported enrichment of Flotillin-1 and LAMP proteins in isolated small EV fractions (Kowal et al., 2016; Lu et al., 2018; Mathieu et al., 2021; Ferreira et al., 2022). In particular, one of these studies reported that “LAMP1-positive subpopulations of EVs represent MVB/lysosome-derived exosomes, which also contain syntenin-1.” Therefore, our choice of EV markers (LAMP2 and Flotillin-1) is consistent with those previously and reliably used to characterize small EVs.

Nevertheless, to further address the reviewer’s concern, we performed additional experiments using a CD63-based fluorescence sensor (CD63-pHluorin), which, combined with TIRF microscopy, enables real-time visualization of CD63-positive exosome release. These experiments were conducted in control and LRRK2-mutant fibroblasts, and the data are presented in new Figure 7 (Panels G-I; Videos 1 and 2). We have also included all relevant references and clarified this point in the revised manuscript.

(3) Indeed, to quantify the amount of certain proteins in EVs, the authors should normalize them by CD63 or CD81.

Protein normalization in isolated EV fractions is indeed challenging. Although tetraspanins such as CD63 and CD81 are commonly enriched in EVs, their abundance can vary considerably across EV subpopulations, cell types, and experimental conditions, making them unreliable as universal normalization markers (Théry et al., J Extracell Vesicles, 2018; Margolis & Sadovsky, Nat Rev Mol Cell Biol, 2019).  Current guidelines from the International Society for Extracellular Vesicles (ISEV), as described in the Minimal Information for Studies of Extracellular Vesicles 2018 (MISEV2018; Théry C, et al. JExtracell Vesicles. 2018, 7:1535750) and updated in MISEV2024 (Welsh JA, et al. J Extracell Vesicles. 2024, 13:e12404), recommend reporting multiple EV markers rather than relying on a single protein for normalization. They also suggest ensuring comparable experimental conditions by using the same number of cells at the start of the experiment and normalizing EV data to cell number or whole-cell lysate protein content at the end of the experiment, among other approaches.

In our study, we normalized EV data to whole-cell lysate (WCL) protein content, as this approach accounts for differences in EV production due to variations in cell number or treatment conditions and is commonly used in the field (Kowal et al., PNAS, 2016; Mathieu et al., Nat Commun, 2021). We also included Flotillin-1 and LAMP2 as EV markers, both of which have been validated as molecular markers of small EV subpopulations.

(4) Hyper normalization in WB quantification in Figure 2E-G is statistically incorrect, as it assumes that one group (in this case, R1441G ctrl) has no variability at all, which is not biologically possible. The authors should repeat the quantification without hypernormalizing one of their groups. This issue is prevalent across the whole manuscript.

We understand the concern regarding “hyper-normalization” (i.e., expressing all values relative to one condition set to 1), which may mask variability in the reference group. However, it is standard practice in immunoblotting analysis to express data relative to a control condition for comparison, as variations in membrane transfer, exposure time, and signal development can differ across blots. In our case, the data are expressed as relative levels (arbitrary units) rather than absolute quantitative values. To facilitate comparison between datasets and account for inter-experimental variation, we continued to express values relative to the mutant LRRK2 MEF condition.

On the other hand, in lipidomics experiments, despite using the same number of seeded cells and identical extraction and analysis protocols, minor biological and technical variability was observed across independent replicates. This variability is inherent to the experimental system and is now explicitly represented in the new table included in Supplemental Figure 1F, which compiles three independent representative lipidomics experiments showing quantitative BMP levels across different conditions.

(5) The authors perform a t-test in Figure 2E-G when comparing more than 2 groups, which is wrong. The authors should use a two-way ANOVA as they are comparing genotype and treatment.

We appreciate the reviewer’s comment and agree with this observation. The MLi-2 and CBE experiments were performed independently and in separate experimental runs; therefore, we have reanalyzed these datasets separately rather than combining them in a two-way ANOVA. To properly compare more than two groups within each dataset, we have now applied a Kruskal-Wallis test followed by an uncorrected Dunn’s post hoc test (Figure 2 D-F and H-J). This non-parametric approach is more appropriate for our data structure, as EV experiments are usually subject to high variability and immunoblot quantifications involving small sample sizes (n≈6) do not always meet the assumptions of normality or equal variance. The Kruskal-Wallis test does not assume normality or equal variances, making it more robust for small, variable biological datasets. The statistical analyses and figure legend have been updated in the revised manuscript accordingly.

In addition, since our CBE treatments yielded statistically non-significant data, we have softened our conclusions throughout the manuscript concerning the contribution of GCase activity to EV-mediated BMP release modulation.

(6) There is a very strong reduction in flotillin-1 in R1441G cells vs WT (Figure 2G) in the EV fraction. That reduction is further exacerbated with MLi2, which likely means it is not kinase activity dependent. Can the authors comment on that?

We agree with the reviewer that Flotillin-1 showed a different behavior compared with LAMP2 in these experiments. As recommended by the MISEV guidelines (Théry C, et al. J Extracell Vesicles. 2018;  7:1535750; Welsh JA, et al. J Extracell Vesicles. 2024, 13:e12404), it is important to analyze more than one EV-associated protein marker. We examined LAMP2, which, together with LAMP1, has been reported to be specifically enriched in EVs of endolysosomal origin (exosomes; Mathieu et al., Nat Commun. 2021, 12:4389 ). In contrast, Flotillin-1 is also associated with small EVs but may represent a distinct EV subpopulation from those positive for LAMP proteins (Kowal J, et al. PNAS 2016, 113:E968-E977).

Nevertheless, the biochemical analysis of isolated EV fractions was complemented by our lipidomics data and, in the revised version, by TIRF microscopy analysis of exosome release in control and G2019S LRRK2 human fibroblasts (new Figure 7, Panels G-I; Videos 1 and 2). In this analysis, we confirmed increased exocytosis of CD63-pHluorin– positive endolysosomes in G2019S LRRK2 human fibroblasts compared to controls, an effect that was reversed by MLi-2 treatment. The CD63-pHluorin–positive compartment of these cells was also largely positive for BMP (new Figure 7G). Collectively, these findings further support the regulatory role of LRRK2 activity in EV-mediated BMP secretion.

(7) In Figure 2C, the authors should express that the LAMP2-EV and flotillin-1 EV fractions from the WB are highly exposed. As presently presented, it is slightly misleading.

We thank the reviewer for this comment. In EV preparations, the amount of protein recovered is typically very low. Therefore, although we loaded all the EV protein obtained from each sample, the immunoblots for LAMP2 and Flotillin-1 in EV fractions required longer exposure times to visualize clear signals across all conditions. We have now indicated in the corresponding figure legend that these EV blots are long-exposure blots to facilitate signal detection and avoid any potential misunderstanding.

(8) If Figure 2C and D are from two different experiments, they should not be plotted together in Figure 2E-G. You cannot compare the effect of MLi2 vs CBE if done in completely different experiments.

We appreciate the reviewer’s comment and agree with this observation. The MLi-2 and CBE experiments were performed independently and in separate experimental runs; therefore, we have reanalyzed these datasets separately rather than combining them in a two-way ANOVA. To properly compare more than two groups within each dataset, we have now applied a Kruskal-Wallis test followed by an uncorrected Dunn’s post hoc test (Figure 2 D-F and H-J). This non-parametric approach is more appropriate for our data structure, as EV experiments are usually subject to high variability and immunoblot quantifications involving small sample sizes (n≈6) do not always meet the assumptions of normality or equal variance. The Kruskal-Wallis test does not assume normality or equal variances, making it more robust for small, variable biological datasets. The revised statistical analyses and figure legends have been updated accordingly in the manuscript.

(9) The authors state that "For the R1441G MEF cells, MLi-2 decreased EV concentration while CBE increased EV particles per ml, in agreement with the effects observed in our biochemical analysis." As Figure S1D shows no statistical significance, the authors don't have sufficient evidence to make this claim.

We apologize for this overstatement. We have revised the text to clarify that, although the differences did not reach statistical significance, a consistent trend toward decreased EV concentration upon MLi-2 treatment and increased EV release following CBE treatment was observed in R1441G MEF cells.

(10) "Altogether, given that BMP is specifically enriched in ILVs (which become exosomes upon release), the data presented above support our biochemical analysis (Figure 2C, D, F) and suggest a role for LRRK2 and GCase in modulating BMP release in association with LAMP2-positive exosomes from MEF cells." As Figure 3E shows no statistical difference of BMP on EVs upon CBE treatment, this sentence is not accurate and should be reframed. Furthermore, the authors claim an increase in EV-LAMP2 in R1441G cells compared to WT, however, the amount of BMP in EVs of R1441G cells vs WT is unchanged with a non-significant reduction. This contradiction does not support the authors' conclusions and really puts into question their whole model.

We thank the reviewer for this observation. After reanalyzing our biochemical data from isolated EV fractions (see new Panels D-F and H-J) using an improved statistical approach, we found that although EV-associated LAMP2 levels were consistently elevated in untreated R1441G LRRK2 MEFs compared to WT cells, CBE treatment only produced a non-significant trend toward increased EV-associated LAMP2 compared to untreated R1441G LRRK2 cells. Accordingly, we have revised the sentence to read as follows:

“Altogether, given that BMP is specifically enriched in ILVs (which become exosomes upon release), the data presented above support our biochemical analysis (Figure 2C, E, G, I) and suggest that LRRK2 activity regulates BMP release in association with LAMP2positive exosomes, whereas GCase activity appears to have a more variable effect under the tested conditions.”

We also agree with the reviewer that, in our MEF model, the amount of BMP in EVs of R1441G cells vs WT is unchanged with a non-significant reduction. However, pharmacological modulation supports our conclusion that BMP release is modulated by LRRK2 activity. Specifically, treatment with the LRRK2 inhibitor MLi-2 decreased EVassociated BMP and LAMP2 levels in R1441G LRRK2 MEFs, and our new data (new Figure 7, Panel G-I; Videos 1 and 2) show increased exocytosis of CD63-pHluorin– positive endolysosomes in G2019S LRRK2 human fibroblasts compared to controls, an effect that was reversed by MLi-2 treatment. The CD63-pHluorin–positive compartment of these cells was also largely positive for BMP (new Figure 7G).

In light of the reviewer’s comment about CBE treatment, we have softened our conclusions throughout the manuscript concerning the contribution of GCase activity in this model.

(11) In Figure 5, 16 h of MLi2 treatment is too long and can lead to off-target effects. I would advise reducing it to 1-4 h.

Prolonged MLi-2 treatments have been extensively used in the field without evidence of significant off-target effects. Several studies, including Fell et al. (2015, J Pharmacol Exp Ther 355:397-409), De Wit et al. (2019, Mol Neurobiol 56:5273-5286), Ho et al. (2022, NPJ Parkinson’s Dis 8:115), Tengberg et al. (2024, Neurobiol Dis 202:106728), and Jaimon et al. (2025, Sci Signal 18:eads5761), have applied long-term (24-48 h) MLi-2 treatments at comparable concentrations without detecting toxicity or off-target alterations, including in MEFs (Ho et al., 2022; Dhekne et al., 2018, eLife 7:e40202). Moreover, the data presented in Figure 5 demonstrate a reduction in CLN5 protein levels in both MEFs and human fibroblasts following MLi-2 treatment, confirming the specificity of the observed effects in LRRK2 mutant cells.

(12) "Our data suggest that BMP is exocytosed in association with EVs and that LRRK2 and GCase activities modulate BMP secretion." Again, cells carrying the R1441G mutation have the same amount of BMP in EVs than WT. This sentence is not factually accurate. Accordingly, CBE did not change the amount of BMP in EVs.

We thank the reviewer for this observation and agree that, in our MEF model, the amount of BMP in EVs from R1441G LRRK2 cells is comparable to that observed in WT cells. However, pharmacological modulation supports our conclusion that BMP release is modulated by LRRK2 activity. Specifically, treatment with the LRRK2 inhibitor MLi-2 decreased EV-associated BMP levels in R1441G LRRK2 MEFs, and our new data (new Figure 7G-I; Videos 1 and 2) show increased exocytosis of CD63-pHluorin–positive endolysosomes in G2019S LRRK2 human fibroblasts compared to controls, an effect that was reversed by MLi-2 treatment. The CD63-pHluorin–positive compartment of these cells was also largely positive for BMP (new Figure 7G). These findings further support the regulatory role of LRRK2 activity in EV-mediated BMP secretion. In addition, in light of the reviewer’s comment about CBE treatment, we have softened our conclusions throughout the paper concerning the contribution of GCase activity in this model.

(13) Figure 6; EV release should have been monitored by more accurate markers such as CD63 and CD81.

We thank the reviewer for this comment. We and others (Kowal et al., 2016; Lu et al., 2018; Mathieu et al., 2021; Ferreira et al., 2022) have reported enrichment of Flotillin-1 and LAMP proteins in isolated small EV fractions. In particular, one of these studies (Mathieu et al., Nat Commun. 2021), in which bafilomycin A1 was also used (to boost exosome release), reported that “LAMP1-positive subpopulations of EVs represent MVB/lysosome-derived exosomes, which also contain syntenin-1.” Altogether, our choice of EV markers (LAMP2 and Flotillin-1) is consistent with those previously and accurately used to characterize EVs. We have now included all relevant references in the revised manuscript to further clarify this point.

(14) Figure 6 suggests that exosomal BMP is controlled by EV release. I would think that is rather obvious.

We agree that the finding that exosomal BMP release is influenced by EV secretion may appear “obvious.” However, our intention in Figure 6 was to provide direct experimental evidence confirming this relationship using pharmacological modulators of EV release. Specifically, inhibition of EV secretion with GW4869 reduced exosomal BMP levels, whereas stimulation with bafilomycin A1 increased them. These data were important to establish a causal link between EV trafficking and BMP export, thereby validating our model and supporting the interpretation that LRRK2 regulates BMP homeostasis through EV-mediated exocytosis, which is further modulated, to some extent, by GCase activity. 

Minor concerns:

(1) Figure 1: Change colors to be color blind friendly.

We thank the reviewer for this helpful suggestion. We have adjusted the colors in Figure 1 to be color-blind friendly. In addition, we have applied the same color-blind friendly palette to the new immunofluorescence data presented in new Figure 7, Panel A and D.

(2) More consistency on "Xmin" vs "X min" would be appreciated.

We thank the reviewer for this observation. We have revised the manuscript to ensure consistent formatting of time indications throughout the text and figures, using the standardized format “X min.”

Reviewer #2 (Recommendations for the authors):

(1)  Figure 2C-D. Were equal amounts of protein loaded in each lane?

Equal protein amounts were loaded in lanes corresponding to whole-cell lysate (WCL) fractions and normalized based on α-Tubulin levels.

For the extracellular vesicle (EV) fractions, all protein recovered from EV pellets after isolation was loaded. In all EV-related experiments, we seeded the same number of EVproducing cells per condition, and the resulting EV-derived data (from both immunoblotting and lipidomics analyses) were normalized to the corresponding whole cell lysate (WCL) protein content to ensure comparability across conditions.

All these technical details have been included in the Materials section of our revised manuscript.

(2) The authors refer to the papers of Medoh et al (ref 43) and Singh et al. (44) for the key role of CLN5 in the BMP biosynthetic pathway. However, Medoh et al reported that CLN5 is the lysosomal BMP synthase. In contrast, Singh et al. reported that PLD3 and PLD4 mediate the synthesis of SS-BMP, and did not find any role for CLN5. 

To avoid any confusion or misinterpretation of our findings regarding CLN5 and given that we do not analyze PLD3 or PLD4 in our study, we have decided to replace the reference to Singh et al. with Bulfon D. et al. (Nat. Commun. 2024, 15:9937) instead. This last work, conducted by an independent group distinct from the one that originally described CLN5, also validated CLN5 as the sole BMP synthase in cells.

Also, authors mention that bafilomycin A1 (B-A1) dramatically boosts EV exocytosis, referring to Kowal et al., 2016 (ref 35) and Lu et al., 2018 (ref 45). However, this is not shown in Kowal et al.

We thank the reviewer for pointing out this mistake. We apologize for the incorrect citation and have now corrected the reference. The statement regarding the effect of bafilomycin A1 on EV exocytosis now appropriately refers to Mathieu et al., 2021 and Lu et al., 2018.

(3) Page 7, it is stated that "No statistically significant differences in intracellular BMP levels were observed in WT LRRK2 MEFs upon LRRK2 or GCase inhibition(Supplemental Figure 1D, E)". The authors probably mean "Supplemental Figure 1F, G"

We thank the reviewer for noting this error. We have corrected the text to refer to panels F and G of Supplemental Figure 1, which correspond to the relevant data. We have also revised the reference to panel I of Supplemental Figure 1 accordingly.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

(1) I have to admit that it took a few hours of intense work to understand this paper and to even figure out where the authors were coming from. The problem setting, nomenclature, and simulation methods presented in this paper do not conform to the notation common in the field, are often contradictory, and are usually hard to understand. Most importantly, the problem that the paper is trying to solve seems to me to be quite specific to the particular memory study in question, and is very different from the normal setting of model-comparative RSA that I (and I think other readers) may be more familiar with.

We have revised the paper for clarity at all levels: motivation, application, and parameterization. We clarify that there is a large unmet need for using RSA in a trial-wise manner, and that this approach indeed offers benefits to any team interested in decoding trial-wise representational information linked to a behavioral responses, and as such is not a problem specific to a single memory study.

(2) The definition of "classical RSA" that the authors are using is very narrow. The group around Niko Kriegeskorte has developed RSA over the last 10 years, addressing many of the perceived limitations of the technique. For example, cross-validated distance measures (Walther et al. 2016; Nili et al. 2014; Diedrichsen et al. 2021) effectively deal with an uneven number of trials per condition and unequal amounts of measurement noise across trials. Different RDM comparators (Diedrichsen et al. 2021) and statistical methods for generalization across stimuli (Schütt et al. 2023) have been developed, addressing shortcomings in sensitivity. Finally, both a Bayesian variant of RSA (Pattern component modelling, (Diedrichsen, Yokoi, and Arbuckle 2018) and an encoding model (Naselaris et al. 2011) can effectively deal with continuous variables or features across time points or trials in a framework that is very related to RSA (Diedrichsen and Kriegeskorte 2017). The author may not consider these newer developments to be classical, but they are in common use and certainly provide the solution to the problems raised in this paper in the setting of model-comparative RSA in which there is more than one repetition per stimulus.

We appreciate the summary of relevant literature and have included a revised Introduction to address this bounty of relevant work. While much is owed to these authors, new developments from a diverse array of researchers outside of a single group can aid in new research questions, and should always have a place in our research landscape. We owe much to the work of Kriegeskorte’s group, and in fact, Schutt et al., 2023 served as a very relevant touchpoint in the Discussion and helped to highlight specific needs not addressed by the assessment of the “representational geometry” of an entire presented stimulus set. Principal amongst these needs is the application of trial-wise representational information that can be related to trial-wise behavioral responses and thus used to address specific questions on brain-behavior relationships. We invite the Reviewer to consider the utility of this shift with the following revisions to the Introduction.

Page 3. “Recently, methodological advancements have addressed many known limitations in cRSA. For example, cross-validated distance measures (e.g., Euclidean distance) have improved the reliability of representational dissimilarities in the presence of noise and trial imbalance (Walther et al., 2016; Nili et al., 2014; Diedrichsen et al., 2021). Bayesian approaches such as pattern component modeling (Diedrichsen, Yokoi, & Arbuckle, 2018) have extended representational approaches to accommodate continuous stimulus features or temporal variation. Further, model comparison RSA strategies (Diedrichsen et al., 2021) and generalization techniques across stimuli (Schütt et al., 2023) have improved sensitivity and inference. Nevertheless, a common feature shared across most of improvements is that they require stimuli repetition to examine the representational structure. This requirement limits their ability to probe brain-behavior questions at the level of individual events”.

Page 8. “While several extensions of RSA have addressed key limitations in noise sensitivity, stimulus variance, and modeling (e.g., Diedrichsen et al., 2021; Schütt et al., 2023), our tRSA approach introduces a new methodological step by estimating representational strength at the trial level. This accounts for the multi-level variance structure in the data, affords generalizability beyond the fixed stimulus set, and allows one to test stimulus- or trial-level modulations of neural representations in a straightforward way”.

Page 44. “Despite such prevalent appreciation for the neurocognitive relevance of stimulus properties, cRSA often does not account for the fact that the same stimulus (e.g., “basketball”) is seen by multiple subjects and produces statistically dependent data, an issue addressed by Schütt et al., 2023, who developed cross validation and bootstrap methods that explicitly model dependence across both subjects and stimulus conditions”.

(3) The stated problem of the paper is to estimate "representational strength" in different regions or conditions. With this, the authors define the correlation of the brain RDM with a model RDM. This metric conflates a number of factors, namely the variances of the stimulus-specific patterns, the variance of the noise, the true differences between different dissimilarities, and the match between the assumed model and the data-generating model. It took me a long time to figure out that the authors are trying to solve a quite different problem in a quite different setting from the model-comparative approach to RSA that I would consider "classical" (Diedrichsen et al. 2021; Diedrichsen and Kriegeskorte 2017). In this approach, one is trying to test whether local activity patterns are better explained by representation model A or model B, and to estimate the degree to which the representation can be fully explained. In this framework, it is common practice to measure each stimulus at least 2 times, to be able to estimate the variance of noise patterns and the variance of signal patterns directly. Using this setting, I would define 'representational strength" very differently from the authors. Assume (using LaTeX notation) that the activity patterns $y_j,n$ for stimulus j, measurement n, are composed of a true stimulus-related pattern ($u_j$) and a trial-specific noise pattern ($e_j,n$). As a measure of the strength of representation (or pattern), I would use an unbiased estimate of the variance of the true stimulus-specific patterns across voxels and stimuli ($\sigma^2_{u}$). This estimator can be obtained by correlating patterns of the same stimuli across repeated measures, or equivalently, by averaging the cross-validated Euclidean distances (or with spatial prewhitening, Mahalanobis distances) across all stimulus pairs. In contrast, the current paper addresses a specific problem in a quite specific experimental design in which there is only one repetition per stimulus. This means that the authors have no direct way of distinguishing true stimulus patterns from noise processes. The trick that the authors apply here is to assume that the brain data comes from the assumed model RDM (a somewhat sketchy assumption IMO) and that everything that reduces this correlation must be measurement noise. I can now see why tRSA does make some sense for this particular question in this memory study. However, in the more common model-comparative RSA setting, having only one repetition per stimulus in the experiment would be quite a fatal design flaw. Thus, the paper would do better if the authors could spell the specific problem addressed by their method right in the beginning, rather than trying to set up tRSA as a general alternative to "classical RSA".

At a general level, our approach rests on the premise that there is meaningful information present in a single presentation of a given stimulus. This assumption may have less utility when the research goals are more focused on estimating the fidelity of signal patterns for RSA, as in designs with multiple repetitions. But it is an exaggeration to state that such a trial-wise approach cannot address the difference between “true” stimulus patterns and noise. This trial-wise approach has explicit utility in relating trial-wise brain information to trial-wise behavior, across multiple cognitions (not only memory studies, as applied here). We have added substantial text to the Introduction distinguishing cRSA, which is widely employed, often in cases with a single repetition per stimulus, and model comparative methods that employ multiple repetitions. We clarify that we do not consider tRSA an alternative to the model comparative approach, and discuss that operational definitions of representational strength are constrained by the study design.

Page 3. “In this paper, we present an advancement termed trial-level RSA, or tRSA, which addresses these limitations in cRSA (not model comparison approaches) and may be utilized in paradigms with or without repeated stimuli”.

Page 4. “Representational geometry usually refers to the structure of similarities among repeated presentations of the same stimulus in the neural data (as captured in the brain RSM) and is often estimated utilizing a model comparison approach, whereas representational strength is a derived measure that quantifies how strongly this geometry aligns with a hypothesized model RSM. In other words, geometry characterizes the pattern space itself, while representational strength reflects the degree of correspondence between that space and the theoretical model under test”.

Finally, we clarified that in our simulation methods we assume a true underlying activity pattern and a random error pattern. The model RSM is computed based on the true pattern, whereas the brain RSM comes from the noisy pattern, not the model RSM itself.

Page 9. “Then, we generated two sets of noise patterns, which were controlled by parameters σ_A and σ_B , respectively, one for each condition”.

(4) The notation in the paper is often conflicting and should be clarified. The actual true and measured activity patterns should receive a unique notation that is distinct from the variances of these patterns across voxels. I assume that $\sigma_ijk$ is the noise variances (not standard deviation)? Normally, variances are denoted with $\sigma^2$. Also, if these are variances, they cannot come from a normal distribution as indicated on page 10. Finally, multi-level models are usually defined at the level of means (i.e., patterns) rather than at the level of variances (as they seem to be done here).

We have added notations for true and measured activity patterns to differentiate it from our notation for variance. We agree that multilevel models are usually defined at the level of means rather than at the level of variances and we include a Figure (Fig 1D) that describes the model in terms of the means. We clarify that the σ ($\sigma$) used in the manuscript were not variances/standard deviations themselves; rather, they were meant to denote components of the actual (multilevel) variance parameter. Each component was sampled from normal distributions, and they collectively summed up to comprise the final variance parameter for each trial. We have modified our notation for each component to the lowercase letter s to minimize confusion. We have also made our R code publicly available on our lab github, which should provide more clarity on the exact simulation process.

(5) In the first set of simulations, the authors sampled both model and brain RSM by drawing each cell (similarity) of the matrix from an independent bivariate normal distribution. As the authors note themselves, this way of producing RSMs violates the constraint that correlation matrices need to be positive semi-definite. Likely more seriously, it also ignores the fact that the different elements of the upper triangular part of a correlation matrix are not independent from each other (Diedrichsen et al. 2021). Therefore, it is not clear that this simulation is close enough to reality to provide any valuable insight and should be removed from the paper, along with the extensive discussion about why this simulation setting is plainly wrong (page 21). This would shorten and clarify the paper.

We have added justification of the mixed-effects model given the potential assumption violations. We caution readers to investigate the robustness of their models, and to employ permutation testing that does not make independence assumptions. We have also added checks of the model residuals and an example of permutation testing in the Appendix. Finally, we agree that the first simulation setting does not possess several properties of realistic RDMs/RSMs; however, we believe that there is utility in understanding the mathematical properties of correlations – an essential component of RSA – in a straightforward simulation where the ground truth is known, thus moving the simulation to Appendix 1.

(6) If I understand the second simulation setting correctly, the true pattern for each stimulus was generated as an NxP matrix of i.i.d. standard normal variables. Thus, there is no condition-specific pattern at all, only condition-specific noise/signal variances. It is not clear how the tRSA would be biased if there were a condition-specific pattern (which, in reality, there usually is). Because of the i.i.d. assumption of the true signal, the correlations between all stimulus pairs within conditions are close to zero (and only differ from it by the fact that you are using a finite number of voxels). If you added a condition-specific pattern, the across-condition RSA would lead to much higher "representational strength" estimates than a within-condition RSA, with obvious problems and biases.

The Reviewer is correct that the voxel values in the true pattern are drawn from i.i.d. standard normal distributions. We take the Reviewer’s suggestion of “condition-specific pattern” to mean that there could be a condition-voxel interaction in two non-mutually exclusive ways. The first is additive, essentially some common underlying multi-voxel pattern like [6, 34, -52, …, 8] for all condition A trials, and different one such pattern for condition B trials, etc. The second is multiplicative, essentially a vector of scaling factors [x1.5, x0.5, x0.8, …, x2.7] for all condition A trials, and a different one such vector for condition B trials, etc. Both possibilities could indeed affect tRSA as much as it would cRSA.

Importantly, If such a strong condition-specific pattern is expected, one can build a condition-specific model RDM using one-shot coding of conditions (see example figure; src: https://www.newbi4fmri.com/tutorial-9-mvpa-rsa), to either capture this interesting phenomenon or to remove this out as a confounding factor. This practice has been applied in multiple regression cRSA approaches (e.g., Cichy et al., 2013) and can also be applied to tRSA.

(7) The trial-level brain RDM to model Spearman correlations was analyzed using a mixed effects model. However, given the symmetry of the RDM, the correlations coming from different rows of the matrix are not independent, which is an assumption of the mixed effect model. This does not seem to induce an increase in Type I errors in the conditions studied, but there is no clear justification for this procedure, which needs to be justified.

We appreciate this important warning, and now caution readers to investigate the robustness of their models, and consider employing permutation testing that does not make independence assumptions. We have also added checks of the model residuals and an example of permutation testing in the supplement.

Page 46. “While linear mixed-effects modeling offers a powerful framework for analyzing representational similarity data, it is critical that researchers carefully construct and validate their models. The multilevel structure of RSA data introduces potential dependencies across subjects, stimuli, and trials, which can violate assumptions of independence if not properly modeled. In the present study, we used a model that included random intercepts for both subjects and stimuli, which accounts for variance at these levels and improves the generalizability of fixed-effect estimates. Still, there is a potential for systematic dependence across trials within a subject. To ensure that the model assumptions were satisfied, we conducted a series of diagnostic checks on an exemplar ROI (right LOC; middle occipital gyrus) in the Object Perception dataset, including visual inspection of residual distributions and autocorrelation (Appendix 3, Figure 13). These diagnostics supported the assumptions of normality, homoscedasticity, and conditional independence of residuals. In addition, we conducted permutation-based inference, similar to prior improvements to cRSA (Niliet al. 2014), using a nested model comparison to test whether the mean similarity in this ROI was significantly greater than zero. The observed likelihood ratio test statistic fell in the extreme tail of the null distribution (Appendix 3, Figure 14), providing strong nonparametric evidence for the reliability of the observed effect. We emphasize that this type of model checking and permutation testing is not merely confirmatory but can help validate key assumptions in RSA modeling, especially when applying mixed-effects models to neural similarity data. Researchers are encouraged to adopt similar procedures to ensure the robustness and interpretability of their findings”.

Exemplar Permutation Testing

To test whether the mean representational strength in the ROI right LOC (middle occipital gyrus) was significantly greater than zero, we used a permutation-based likelihood ratio test implemented via the permlmer function. This test compares two nested linear mixed-effects models fit using the lmer function from the lme4 package, both including random intercepts for Participant and Stimulus ID to account for between-subject and between-item variability.

The null model excluded a fixed intercept term, effectively constraining the mean similarity to zero after accounting for random effects:

ROI ~ 0 + (1 | Participant) + (1 | Stimulus)

The full model included the same random effects structure but allowed the intercept to be freely estimated:

ROI ~ 1 + (1 | Participant) + (1 | Stimulus)

By comparing the fit of these two models, we directly tested whether the average similarity in this ROI was significantly different from zero. Permutation testing (1,000 permutations) was used to generate a nonparametric p-value, providing inference without relying on normality assumptions. The full model, which estimated a nonzero mean similarity in the right LOC (middle occipital gyrus), showed a significantly better fit to the data than the null model that fixed the mean at zero (χ²(1) = 17.60, p = 2.72 × 10⁻⁵). The permutation-based p-value obtained from permlmer confirmed this effect as statistically significant (p = 0.0099), indicating that the mean similarity in this ROI was reliably greater than zero. These results support the conclusion that the right LOC contains representational structure consistent with the HMAXc2 RSM. A density plot of the permuted likelihood ratio tests is plotted along with the observed likelihood ratio test in Appendix 3 Figure 14.

(8) For the empirical data, it is not clear to me to what degree the "representational strength" of cRSA and tRSA is actually comparable. In cRSA, the Spearman correlation assesses whether the distances in the data RSM are ranked in the same order as in the model. For tRSA, the comparison is made for every row of the RSM, which introduces a larger degree of flexibility (possibly explaining the higher correlations in the first simulation). Thus, could the gains presented in Figure 7D not simply arise from the fact that you are testing different questions? A clearer theoretical analysis of the difference between the average row-wise Spearman correlation and the matrix-wise Spearman correlation is urgently needed. The behavior will likely vary with the structure of the true model RDM/RSM.

We agree that the comparability between mean row-wise Spearman correlations and the matrix-wise Spearman correlation is needed. We believe that the simulations are the best approach for this comparison, since they are much more robust than the empirical dataset and have the advantage of knowing the true pattern/noise levels. We expand on our comparison of mean tRSA values and matrix-wise Spearman correlations on page 42.

Page 42. “Although tRSA and cRSA both aim to quantify representational strength, they differ in how they operationalize this concept. cRSA summarizes the correspondence between RSMs as a single measure, such as the matrix-wise Spearman correlation. In contrast, tRSA computes such correspondence for each trial, enabling estimates at the level of individual observations. This flexibility allows trial-level variability to be modeled directly, but also introduces subtle differences in what is being measured. Nonetheless, our simulations showed that, although numerical differences occasionally emerged—particularly when comparing between-condition tRSA estimates to within-condition cRSA estimates—the magnitude of divergence was small and did not affect the outcome of downstream statistical tests”.

(9) For the real data, there are a number of additional sources of bias that need to be considered for the analysis. What if there are not only condition-specific differences in noise variance, but also a condition-specific pattern? Given that the stimuli were measured in 3 different imaging runs, you cannot assume that all measurement noise is i.i.d. - stimuli from the same run will likely have a higher correlation with each other.

We recognize the potential of condition-specific patterns and chose to constrain the analyses to those most comparable with cRSA. However, depending on their hypotheses, researchers may consider testing condition RSMs and utilizing a model comparison approach or employ the z-scored approach, as employed in the simulations above. Regarding the potential run confounds, this is always the case in RSA and why we exclude within-run comparisons. We have also added to the Discussion the suggestion to include run as a covariate in their mixed-effects models. However, we do not employ this covariate here as we preferred the most parsimonious model to compare with cRSA.

Page 46 - 47. “Further, while analyses here were largely employed to be comparable with cRSA, researchers should consider taking advantage of the flexibility of the mixed-effects models and include co variates of non-interest (run, trial order etc.)”.

(10) The discussion should be rewritten in light of the fact that the setting considered here is very different from the model-comparative RSA in which one usually has multiple measurements per stimulus per subject. In this setting, existing approaches such as RSA or PCM do indeed allow for the full modelling of differences in the "representational strength" - i.e., pattern variance across subjects, conditions, and stimuli.

We agree that studies advancing designs with multiple repetitions of a given stimulus image are useful in estimating the reliability of concept representations. We would argue however that model comparison in RSA is not restricted to such data. Many extant studies do not in fact have multiple repetitions per stimulus per subject (Wang et al., 2018 https://doi.org/10.1088/1741-2552/abecc3, Gao et al, 2022 https://doi.org/10.1093/cercor/bhac058, Li et al, 2022 https://doi.org/10.1002/hbm.26195, Staples & Graves, 2020 https://doi.org/10.1162/nol_a_00018) that allow for that type of model-comparative approach. While beneficial in terms of noise estimation, having multiple presentations was not a requirement for implementing cRSA (Kriegeskorte, 2008 https://doi.org/10.3389/neuro.06.004.2008). The aim of this manuscript is to introduce the tRSA approach to the broad community of researchers whose research questions and datasets could vary vastly, including but not limited to the number of repeated presentations and the balance of trial counts across conditions.

(11) Cross-validated distances provide a powerful tool to control for differences in measurement noise variances and possible covariances in measurement noise across trials, which has many distinct advantages and is conceptually very different from the approach taken here.

We have added language on the value of cross-validation approaches to RSA in the Discussion:

Page 47. “Additionally, we note that while our proposed tRSA framework provides a flexible and statistically principled approach for modeling trial-level representational strength, we acknowledge that there are alternative methods for addressing trial-level variability in RSA. In particular, the use of cross-validated distance metrics (e.g., crossnobis distance) has become increasingly popular for controlling differences in measurement noise variance and accounting for possible covariance structures across trials (Walther et al., 2016). These metrics offer several advantages, including unbiased estimation of representational dissimilarities under Gaussian noise assumptions and improved generalization to unseen data. However, cross-validated distances are conceptually distinct from the approach taken here: whereas cross-validation aims to correct for noise-related biases in representational dissimilarity matrices, our trial-level RSA method focuses on estimating and modeling the variability in representation strength across individual trials using mixed-effects modeling. Rather than proposing a replacement for cross-validated RSA, tRSA adds a complementary tool to the methodological toolkit—one that supports hypothesis-driven inference about condition effects and trial-level covariates, while leveraging the full structure of the data”.

(12) One of the main limitations of tRSA is the assumption that the model RDM is actually the true brain RDM, which may not be the case. Thus, in theory, there could be a different model RDM, in which representational strength measures would be very different. These differences should be explained more fully, hopefully leading to a more accessible paper.

Indeed, the chosen model RSM may not be the true RSM, but as the noise level increases the correlation between RSMs practically becomes zero. In our simulations we assume this to be true as a straightforward way to manipulate the correspondence between the brain data and the model. However, just like cRSA, tRSA is constrained by the model selections the researchers employ. We encourage researchers to have carefully considered theoretically-motivated models and, if their research questions require, consider multiple and potentially competing models. Furthermore, the trial-wise estimates produced by tRSA encourage testing competing models within the multiple regression framework. We have added this language to the Discussion.

Page 46. ..”choose their model RSMs carefully. In our simulations, we designed our model RSM to be the “true” RSM for demonstration purposes. However, researchers should consider if their models and model alternatives”.

Pages 45-46. “While a number of studies have addressed the validity of measuring representational geometry using designs with multiple repetitions, a conceptual benefit of the tRSA approach is the reliance on a regression framework that engenders the testing of competing conceptual models of stimulus representation (e.g., taxonomic vs. encyclopedic semantic features, as in Davis et al., 2021)”.

Reviewer #2 (Public review):

(1)  While I generally welcome the contribution, I take some issue with the accusatory tone of the manuscript in the Introduction. The text there (using words such as 'ignored variances', 'errouneous inferences', 'one must', 'not well-suited', 'misleading') appears aimed at turning cRSA in a 'straw man' with many limitations that other researchers have not recognized but that the new proposed method supposedly resolves. This can be written in a more nuanced, constructive manner without accusing the numerous users of this popular method of ignorance.

We apologize for the unintended accusatory tone. We have clarified the many robust approaches to RSA and have made our Introduction and Discussion more nuanced throughout (see also 3, 11 and16).

(2) The described limitations are also not entirely correct, in my view: for example, statistical inference in cRSA is not always done using classic parametric statistics such as t-tests (cf Figure 1): the rsatoolbox paper by Nili et al. (2014) outlines non-parametric alternatives based on permutation tests, bootstrapping and sign tests, which are commonly used in the field. Nor has RSA ever been conducted at the row/column level (here referred to by the authors as 'trial level'; cf King et al., 2018).

We agree there are numerous methods that go beyond cRSA addressing these limitations and have added discussion of them into our manuscript as well as an example analysis implementing permutation tests on tRSA data (see response to 7). We thank the reviewer for bringing King et al., 2014 and their temporal generalization method to our attention, we added reference to acknowledge their decoding-based temporal generalization approach.

Page 8. “It is also important to note that some prior work has examined similarly fine-grained representations in time-resolved neuroimaging data, such as the temporal generalization method introduced by King et al. (see King & Dehaene, 2014). Their approach trains classifiers at each time point and tests them across all others, resulting in a temporal generalization matrix that reflects decoding accuracy over time. While such matrices share some structural similarity with RSMs, they do not involve correlating trial-level pattern vectors with model RSMs nor do their second-level models include trial-wise, subject-wise, and item-wise variability simultaneously”.

(3) One of the advantages of cRSA is its simplicity. Adding linear mixed effects modeling to RSA introduces a host of additional 'analysis parameters' pertaining to the choice of the model setup (random effects, fixed effects, interactions, what error terms to use) - how should future users of tRSA navigate this?

We appreciate the opportunity to offer more specific proscriptions for those employing a tRSA technique, and have added them to the Discussion:

Page 46. “While linear mixed-effects modeling offers a powerful framework for analyzing representational similarity data, it is critical that researchers carefully construct and validate their models and choose their model RSMs carefully. In our simulations, we designed our model RSM to be the “true” RSM for demonstration purposes. However, researchers should consider if their models and model alternatives. However, researchers should always consider if their models match the goals of their analysis, including 1) constructing the random effects structure that will converge in their dataset and 2) testing their model fits against alternative structures (Meteyard & Davies, 2020; Park et al., 2020) and 3) considering which effects should be considered random or fixed depending on their research question”.

(4) Here, only a single real fMRI dataset is used with a quite complicated experimental design for the memory part; it's not clear if there is any benefit of using tRSA on a simpler real dataset. What's the benefit of tRSA in classic RSA datasets (e.g., Kriegeskorte et al., 2008), with fixed stimulus conditions and no behavior?

To clarify, our empirical approach uses two different tasks: an Object Perception task more akin to the classic RSA datasets employing passive viewing, and a Conceptual Retrieval task that more directly addresses the benefits of the trialwise approach. We felt that our Object Perception dataset is a simpler empirical fMRI dataset without explicit task conditions or a dichotomous behavioral outcome, whereas the Retrieval dataset is more involved (though old/new recognition is the most common form of memory retrieval testing) and  dependent on behavioral outcomes. However, we recognize the utility of replication from other research groups and do invite researchers to utilize tRSA on their datasets.

(5) The cells of an RDM/RSM reflect pairwise comparisons between response patterns (typically a brain but can be any system; cf Sucholutsky et al., 2023). Because the response patterns are repeatedly compared, the cells of this matrix are not independent of one another. Does this raise issues with the validity of the linear mixed effects model? Does it assume the observations are linearly independent?

We recognize the potential danger for not meeting model assumptions. Though our simulation results and model checks suggest this is not a fatal flaw in the model design, we caution readers to investigate the robustness of their models, and consider employing permutation testing that does not make independence assumptions. We have also added checks of the model residuals and an example of permutation testing in the Appendix. See response to R1.

(6) The manuscript assumes the reader is familiar with technical statistical terms such as Type I/II error, sensitivity, specificity, homoscedasticity assumptions, as well as linear mixed models (fixed effects, random effects, etc). I am concerned that this jargon makes the paper difficult to understand for a broad readership or even researchers currently using cRSA that might be interested in trying tRSA.

We agree this jargon may cause the paper to be difficult to understand. We have expanded/added definitions to these terms throughout the methods and results sections.

Page 12. “Given data generated with 𝑠_{𝑐𝑜𝑛𝑑,𝐴} = 𝑠_{𝑐𝑜𝑛𝑑,B}, the correct inference should be a failure to reject the null hypothesis of ; any significant () result in either direction was considered a false positive (spurious effect, or Type I error). Given data generated with , the inference was considered correct if it rejected the null hypothesis of  and yielded the expected sign of the estimated contrast (b_B-𝐴<0). A significant result with the reverse sign of the estimated contrast (b_B-𝐴<0) was considered a Type I error, and a nonsignificant (𝑝 ≥ 0.05) result was considered a false negative (failure to detect a true effect, or Type II error)”.

Page 2. “Compared to cRSA, the multi-level framework of tRSA was both more theoretically appropriate and significantly sensitive (better able to detect) to true effects”.

Page 25.”The performance of cRSA and tRSA were quantified with their specificity (better avoids false positives, 1 - Type I error rate) and sensitivity (better avoids false negatives 1 - Type II error rate)”.

Page 6. “One of the fundamental assumptions of general linear models (step 4 of cRSA; see Figure 1D) is homoscedasticity or homogeneity of variance — that is, all residuals should have equal variance” .

Page11. “Specifically, a linear mixed-effects model with a fixed effect  of condition (which estimates the average effect across the entire sample, capturing the overall effect of interest) and random effects of both subjects and stimuli (which model variation in responses due to differences between individual subjects and items, allowing generalization beyond the sample) were fitted to tRSA estimates via the `lme4 1.1-35.3` package in R (Bates et al., 2015), and p-values were estimated using Satterthwaites’s method via the `lmerTest 3.1-3` package (Kuznetsova et al., 2017)”.

(7) I could not find any statement on data availability or code availability. Given that the manuscript reuses prior data and proposes a new method, making data and code/tutorials openly available would greatly enhance the potential impact and utility for the community.

We thank the reviewer for raising our oversight here. We have added our code and data availability statements.

Page 9. “Data is available upon request to the corresponding author and our simulations and example tRSA code is available at https://github.com/electricdinolab”.

Reviewer #1 (Recommendations for the authors):

(13) Page 4: The limitations of cRSA seem to be based on the assumption that within each different experimental condition, there are different stimuli, which get combined into the condition. The framework of RSA, however, does not dictate whether you calculate a condition x condition RDM or a larger and more complete stimulus x stimulus RDM. Indeed, in practice we often do the latter? Or are you assuming that each stimulus is only shown once overall? It would be useful at this point to spell out these implicit assumptions.

We agree that stimulus x stimulus RDMs can be constructed and are often used. However, as we mentioned in the Introduction, researchers are often interested in the difference between two (or more) conditions, such as “remembered” vs. “forgotten” (Davis et al., https://doi.org/10.1093/cercor/bhaa269) or “high cognitive load” vs. “low cognitive load” (Beynel et al., https://doi.org/10.1523/JNEUROSCI.0531-20.2020). In those cases, the most common practice with cRSA is to construct condition-specific RDMs, compute cRSA scores separately for each condition, and then compare the scores at the group level. The number of times each stimulus gets presented does not prevent one from creating a model RDM that has the same rows and columns as the brain RDM, either in the same condition (“high load”) or across different conditions.

(14) Page 5: The difference between condition-level and stimulus-level is not clear. Indeed, this definition seems to be a function of the exact experimental design and is certainly up for interpretation. For example, if I conduct a study looking at the activity patterns for 4 different hand actions, each repeated multiple times, are these actions considered stimuli or conditions?

We have added clarifying language about what is considered stimuli vs conditions. Indeed, this will depend on the specific research questions being employed and will affect how researchers construct their models. In this specific example, one would most likely consider each different hand action a condition, treating them as fixed effects rather than random effects, given their very limited number and the lack of need to generalize findings to the broader “hand actions” category.

Page 5. “Critically, the distinction between condition-level and stimulus level is not always clear as researchers may manipulate stimulus-level features themselves. In these cases, what researchers ultimately consider condition-level and stimulus-level will depend on their specific research questions. For example, researchers intending to study generalized object representation may consider object category a stimulus-level feature, while researchers interested in if/how object representation varies by category may consider the same category variable condition-level”.

(15) Page 5: The fact that different numbers of trials / different levels of measurement noise / noise-covariance of different conditions biases non-cross-validated distances is well known and repeatedly expressed in the literature. We have shown that cross-validation of distances effectively removes such biases - of course, it does not remove the increased estimation variability of these distances (for a formal analysis of estimation noise on condition patterns and variance of the cross-nobis estimator, see (Diedrichsen et al. 2021)).

We thank the reviewer for drawing our attention to this literature and have added discussions of these methods.

(16). Page 5: "Most studies present subjects with a fixed set of stimuli, which are supposedly samples representative of some broader category". This may be the case for a certain type of RSA experiments in the visual domain, but it would be unfair to say that this is a feature of RSA studies in general. In most studies I have been involved in, we use a "stimulus" x "stimulus" RDM.

We have edited this sentence to avoid the “most” characterization. We also added substantial text to the introduction and discussion distinguishing cRSA, which is nonetheless widely employed, especially in cases with a single repetition per stimulus (Macklin et al., 2023, Liu et al, 2024) and the model comparative method and explicitly stating that we do not consider tRSA an alternative to the model comparative approach.

(17). Page 5: I agree that "stimuli" should ideally be considered a random effect if "stimuli" can be thought of as sampled from a larger population and one wants to make inferences about that larger population. Sometimes stimuli/conditions are more appropriately considered a fixed effect (for example, when studying the response to stimulation of the 5 fingers of the right hand). Techniques to consider stimuli/conditions as a random effect have been published by the group of Niko Kriegeskorte (Schütt et al. 2023).

Indeed, in some cases what may be thought of as “stimuli” would be more appropriately entered into the model as a fixed effect; such questions are increasingly relevant given the focus on item-wise stimulus properties (Bainbridge et al., Westfall & Yarkoni). We have added text on this issue to the Discussion and caution researchers to employ models that most directly answer their research questions.

Page 46. “However, researchers should always consider if their models match the goals of their analysis, including 1) constructing the random effects structure that will converge in their dataset and 2) testing their model fits against alternative structures (Meteyard & Davies, 2020; Park et al., 2020) and 3) considering which effects should be considered random or fixed depending on their research question. An effect is fixed when the levels represent the specific conditions of theoretical interest (e.g., task condition) and the goal is to estimate and interpret those differences directly. In contrast, an effect is random when the levels are sampled from a broader population (e.g., subjects) and the goal is to account for their variability while generalizing beyond the sample tested. Note that the same variable (e.g., stimuli) may be considered fixed or random depending on the research questions”.

(18) Page 6: It is correct that the "classical" RSA depends on a categorical assignment of different trials to different stimuli/conditions, such that a stimulus x stimulus RDM can be computed. However, both Pattern Component Modelling (PCM) and Encoding models are ideally set up to deal with variables that vary continuously on a trial-by-trial or moment-by-moment basis. tRSA should be compared to these approaches, or - as it should be clarified - that the problem setting is actually quite a different one.

We agree that PCM and encoding models offer a flexible approach and handle continuous trial-by-trial variables. We have clarified the problem setting in cRSA is distinct on page 6, and we have added the robustness of encoding models and their limitations to the Discussion.

Page 6. “While other approaches such as Pattern Component Modeling (PCM) (Diedrichsen et al., 2018) and encoding models (Naselaris et al., 2011) are well-suited to analyzing variables that vary continuously on a trial-by-trial or moment-by-moment basis, these frameworks address different inferential goals. Specifically, PCM and encoding models focus on estimating variance components or predicting activation from features, while cRSA is designed to evaluate representational geometry. Thus, cRSA as well as our proposed approach address a problem setting distinct from PCM and encoding models”.

(19) Page 8: "Then, we generated two noise patterns, which were controlled by parameters 𝜎 𝐴 and 𝜎𝐵, respectively, one for each condition." This makes little sense to me. The noise patterns should be unique to each trial - you should generate n_a + n_b noise patterns, no?

We clarify that the “noise patterns” here are n_voxel x n_trial in size; in other words, all trial-level noise patterns are generated together and each trial has their own unique noise pattern. We have revised our description as “two sets of noise patterns” for clarity starting on page 9.

(20) Page 9: First, I assume if this is supposed to be a hierarchical level model, the "noise parameters" here correspond to variances? Or do these \sigma values mean to signify standard deviations? The latter would make little sense. Or is it the noise pattern itself?

As clarified in 4., the σ values are meant to denote hierarchical components of the composite standard deviation; we have updated our notation to use lower case letter s instead for clarity.

(21) Page 10: your formula states "𝜎_{𝑠𝑢𝑏𝑗}~ 𝙽(0, 0.5^2)". This conflicts with your previous mention that \sigmas are noise "levels" are they the noise patterns themselves now? Variances cannot be normally distributed, as they cannot be negative.

As clarified in 4., the σ values are meant to denote hierarchical components of the composite standard deviation; we have updated our notation to use lower case letter s instead for clarity.

(22) Page 13: What was the task of the subject in the Memory retrieval task? Old/new judgements relative to encoding of object perception?

We apologize for the lack of clarity about the Memory Retrieval task and have added that information and clarified that the old/new judgements were relative to a separate encoding phase, the brain data for which has been reported elsewhere.

Page 14. “Memory Retrieval took place one day after Memory Encoding and involved testing participants’ memory of the objects seen in the Encoding phase. Neural data during the Encoding phase has been reported elsewhere. In the main Memory Retrieval task, participants were presented with 144 labels of real-world objects, of which 114 were labels for previously seen objects and 30 were unrelated novel distractors. Participants performed old/new judgements, as well as their confidence in those judgements on a four-point scale (1 = Definitely New, 2 = Probably New, 3 = Probably Old, 4 = Definitely Old)”.

(23) Page 13: If "Memory Retrieval consisted of three scanning runs", then some of the stimulus x stimulus correlations for the RSM must have been calculated within a run and some between runs, correct? Given that all within-run estimates share a common baseline, they share some dependence. Was there a systematic difference between the within-run and the between-run correlations?

We have clarified in this portion of the methods that within run comparisons were excluded from our analyses. We also double-checked that the within-run exclusion was included in the description of the Neural RSMs.

Page 14. “Retrieval consisted of three scanning runs, each with 38 trials, lasting approximately 9 minutes and 12 seconds (within-run comparisons were later excluded from RSA analyses)”.

Page 18. “This was done by vectorizing the voxel-level activation values within each region and calculating their correlations using Pearson’s r, excluding all within-run comparisons.”

(24) Page 20: It is not clear why the mean estimate of "representational strength" (i.e., model-brain RSM correlations) is important at all. This comes back to Major point #2, namely that you are trying to solve a very different problem from model-comparative RSA.

We have clarified that our approach is not an alternative to model-comparative RSA, and that depending on the task constraints researchers may choose to compare models with tRSA or other approaches requiring stimulus repetition (see 3).

(25) Page 21: I believe the problems of simulating correlation matrices directly in the way that the authors in their first simulation did should be well known and should be moved to an appendix at best. Better yet, the authors could start with the correct simulation right away.

We agree the paper is more concise with these simulations being moved to the appendix and more briefly discussed. We have implemented these changes (Appendix 1). However, we are not certain that this problem is unknown, and have several anecdotes of researchers inquiring about this “alternative” approach in talks with colleagues, thus we do still discuss the issues with this method.

(26) Page 26: Is the "underlying continuous noise variable 𝜎𝑡𝑟𝑖𝑎𝑙 that was measured by 𝑣𝑚𝑒𝑎𝑠𝑢𝑟𝑒𝑑 " the variance of the noise pattern or the noise pattern itself? What does it mean it was "measured" - how?

𝜎𝑡𝑟𝑖𝑎𝑙 is a vector of standard deviations for different trials, and 𝜎𝑡𝑟𝑖𝑎𝑙 i would be used to generate the noise patterns for trial i. v_measured is a hypothetical measurement of trial-level variability, such as “memorability” or “heartbeat variability”. We have revised our description to clarify our methods.

Reviewer #2 (Recommendations for the authors):

(8) It would be helpful to provide more clarity earlier on in the manuscript on what is a 'trial': in my experience, a row or column of the RDM is usually referred to as 'stimulus condition', which is typically estimated on multiple trials (instances or repeats) of that stimulus condition (or exemplars from that stimulus class) being presented to the subject. Here, a 'trial' is both one measurement (i.e., single, individual presentation of a stimulus) and also an entry in the RDM, but is this the most typical scenario for cRSA? There is a section in the Discussion that discusses repetitions, but I would welcome more clarity on this from the get-go.

We have added discussion of stimulus repetition methods and datasets to the Introduction and clarified our use of the terms.

Page 8. “Critically, in single-presentation designs, a “trial” refers to one stimulus presentation, and corresponds to a row or column in the RSM. In studies with repeated stimuli, these rows are often called “conditions” and may reflect aggregated patterns across trials. tRSA is compatible with both cases: whether rows represent individual trials or averaged trials that create “conditions”, tRSA estimates are computed at the row level”.

(9) The quality of the results figures can be improved. For example, axes labels are hard to read in Figure 3A/B, panels 3C/D are hard to read in general. In Figure 7E, it's not possible to identify the 'dark red' brain regions in addition to the light red ones.

We thank the reviewer for raising these and have edited the figures to be more readable in the manner suggested.

(10) I would be interested to see a comparison between tRSA and cRSA in other fMRI (or other modality) datasets that have been extensively reported in the literature. These could be the original Kriegeskorte 96 stimulus monkey/fMRI datasets, commonly used open datasets in visual perception (e.g., THINGS, NSD), or the above-mentioned King et al. dataset, which has been analyzed in various papers.

We recognize the great utility of replication from other research groups and do invite researchers to utilize tRSA on their datasets.

(11) On P39, the authors suggest 'researchers can confidently replace their existing cRSA analysis with tRSA': Please discuss/comment on how researchers should navigate the choice of modeling parameters in tRSA's linear mixed effects setting.

We have added discussion of the mixed-effects parameters and the various and encourage researchers to follow best practices for their model selection.

Page 46. “However, researchers should always consider if their models match the goals of their analysis, including 1) constructing the random effects structure that will converge in their dataset and 2) testing their model fits against alternative structures (Meteyard & Davies, 2020; Park et al., 2020) and 3) considering which effects should be considered random or fixed depending on their research question”.

(12) The final part of the Results section, demonstrating the tRSA results for the continuous memorability factor in the real fMRI data, could benefit from some substantiation/elaboration. It wasn't clear to me, for example, to what extent the observed significant association between representational strength and item memorability in this dataset is to be 'believed'; the Discussion section (p38). Was there any evidence in the original paper for this association? Or do we just assume this is likely true in the brain, based on prior literature by e.g. Bainbridge et al (who probably did not use tRSA but rather classic methods)?

Indeed, memorability effects have been replicated in the literature, but not using the tRSA method. We have expanded our discussion to clarify the relationship of our findings and the relevant literature and methods it has employed.

Page 38. “Critically, memorability is a robust stimulus property that is consistent across participants and paradigms (Bainbridge, 2022). Moreover, object memorability effects have been replicated using a variety of methods aside from tRSA, including univariate analyses and representational analyses of neural activity patterns where trial-level neural activity pattern estimates are correlated directly with object memorability (Slayton et al, 2025).”

(13) The abstract could benefit from more nuance; I'm not sure if RSA can indeed be said to be 'the principal method', and whether it's about assessing 'quality' of representations (more commonly, the term 'geometry' or 'structure' is used).

We have edited the abstract to reflect the true nuisance in the current approaches.

Abstract. Neural representation refers to the brain activity that stands in for one’s cognitive experience, and in cognitive neuroscience, a prominent method of studying neural representations is representational similarity analysis (RSA). While there are several recent advances in RSA, the classic RSA (cRSA) approach examines the structure of representations across numerous items by assessing the correspondence between two representational similarity matrices (RSMs): usually one based on a theoretical model of stimulus similarity and the other based on similarity in measured neural data.

(14) RSA is also not necessarily about models vs. neural data; it can also be between two neural systems (e.g., monkey vs. human as in Kriegeskorte et al., 2008) or model systems (see Sucholutsky et al., 2023). This statement is also repeated in the Introduction paragraph 1 (later on, it is correctly stated that comparing brain vs. model is most likely the 'most common' approach).

We have added these examples in our introduction to RSA.

Page 3.”One of the central approaches for evaluating information represented in the brain is representational similarity analysis (RSA), an analytical approach that queries the representational geometry of the brain in terms of its alignment with the representational geometry of some cognitive model (Kriegeskorte et al., 2008; Kriegeskorte & Kievit, 2013), or, in some cases, compares the representational geometry of two neural systems (e.g., Kriegeskorte et al., 2008) or two model systems (Sucholutsky et al., 2023)”.

(15) 'theoretically appropriate' is an ambiguous statement, appropriate for what theory?

We apologize for the ambiguous wording, and have corrected the text:

Page 11. “Critically, tRSA estimates were submitted to a mixed-effects model which is statistically appropriate for modeling the hierarchical structure of the data, where observations are nested within both subjects and stimuli (Baayen et al., 2008; Chen et al., 2021)”.

(16) I found the statement that cRSA "cannot model representation at the level of individual trials" confusing, as it made me think, what prohibits one from creating an RDM based on single-trial responses? Later on, I understood that what the authors are trying to say here (I think) is that cRSA cannot weigh the contributions of individual rows/columns to the overall representational strength differently.

We thank the reviewer for their clarifying language and have added it to this section of the manuscript.

“Abstract. However, because cRSA cannot weigh the contributions of individual trials (RSM rows/columns), it is fundamentally limited in its ability to assess subject-, stimulus-, and trial-level variances that all influence representation”.

(17) Why use "RSM" instead of "RDM"? If the pairwise comparison metric is distance-based (e..g, 1-correlation as described by the authors), RDM is more appropriate.

We apologize for the error, and have clarified the Methods text:

Page3-4. First, brain activity responses to a series of N trials are compared against each other (typically using Pearson’s r) to form an N×N representational similarity matrix.

(18) Figure 2: please write 'Correlation estimate' in the y-axis label rather than 'Estimate'.

We have edited the label in Figure 2.

(19) Page 6 'leaving uncertain the directionality of any findings' - I do not follow this argument. Obviously one can generate an RDM or RSM from vector v or vector -v. How does that invalidate drawing conclusions where one e.g., partials out the (dis)similarity in e.g., pleasantness ratings out of another RDM/RSM of interest?

We agree such an approach does not invalidate the partial method; we have clarified what we mean by “directionality”.

Page 8. ”For instance, even though a univariate random variable , such as pleasantness ratings, can be conveniently converted to an RSM using pairwise distance metrics (Weaverdyck et al., 2020), the very same RSM would also be derived from the opposite random variable , leaving uncertain of the directionality (or if representation is strongest for pleasant or unpleasant items) of any findings with the RSM (see also Bainbridge & Rissman, 2018)”.

(20) P7 'sampled 19900 pairs of values from a bi-variate normal distribution', but the rows/columns in an RDM are not independent samples - shouldn't this be included in the simulation? I.e., shouldn't you simulate first the n=200 vectors, and then draw samples from those, as in the next analysis?

This section has been moved to Appendix 1 (see responses to Reviewer 1.13).

(21) Under data acquisition, please state explicitly that the paper is re-using data from prior experiments, rather than collecting data anew for validating tRSA.

We have clarified this in the data acquisition section.

Page 13. “A pre-existing dataset was analyzed to evaluate tRSA. Main study findings have been reported elsewhere (S. Huang, Bogdan, et al., 2024)”.

(22) Figure 4 could benefit from some more explanation in-text. It wasn't clear to me, for example, how to interpret the asterisks depicted in the right part of the figure.

We clarified the meaning of the asterisks in the main text in addition to the existent text in the figure caption.

Page 26. “see Figure 4, off-diagonal cells in blue; asterisks indicate where tRSA was statistically more sensitive then cRSA)”.

(23) Page 38 "the outcome of tRSA's improved characterization can be seen in multiple empirical outcomes:" it seems there is one mention of 'outcomes' too many here.

We have revised this sentence.

Page 41. “tRSA's improved characterization can be seen in multiple empirical outcomes”.

(24) Page 38 "model fits became the strongest" it's not clear what aspect of the reported results in the paragraph before this is referring to - the Appendix?

Yes, the model fits are in the Appendix, we have added this in text citation.

Moreover, model-fits became the strongest when the models also incorporated trial-level variables such as fMRI run and reaction time (Appendix 3, Table 6).

References

Diedrichsen, J., Berlot, E., Mur, M., Schütt, H. H., Shahbazi, M., & Kriegeskorte, N. (2021). Comparing representational geometries using whitened unbiased-distance-matrix similarity. Neurons, Behavior, Data and Theory, 5(3). https://arxiv.org/abs/2007.02789

Diedrichsen, J., & Kriegeskorte, N. (2017). Representational models: A common framework for understanding encoding, pattern-component, and representational-similarity analysis. PLoS Computational Biology, 13(4), e1005508.

Diedrichsen, J., Yokoi, A., & Arbuckle, S. A. (2018). Pattern component modeling: A flexible approach for understanding the representational structure of brain activity patterns. NeuroImage, 180, 119-133.

Naselaris, T., Kay, K. N., Nishimoto, S., & Gallant, J. L. (2011). Encoding and decoding in fMRI. NeuroImage, 56(2), 400-410.

Nili, H., Wingfield, C., Walther, A., Su, L., Marslen-Wilson, W., & Kriegeskorte, N. (2014). A toolbox for representational similarity analysis. PLoS Computational Biology, 10(4), e1003553.

Schütt, H. H., Kipnis, A. D., Diedrichsen, J., & Kriegeskorte, N. (2023). Statistical inference on representational geometries. ELife, 12. https://doi.org/10.7554/eLife.82566

Walther, A., Nili, H., Ejaz, N., Alink, A., Kriegeskorte, N., & Diedrichsen, J. (2016). Reliability of dissimilarity measures for multi-voxel pattern analysis. NeuroImage, 137, 188-200.

King, M. L., Groen, I. I., Steel, A., Kravitz, D. J., & Baker, C. I. (2019). Similarity judgments and cortical visual responses reflect different properties of object and scene categories in naturalistic images. NeuroImage, 197, 368-382.

Kriegeskorte, N., Mur, M., Ruff, D. A., Kiani, R., Bodurka, J., Esteky, H., ... & Bandettini, P. A. (2008). Matching categorical object representations in inferior temporal cortex of man and monkey. Neuron, 60(6), 1126-1141.

Nili, H., Wingfield, C., Walther, A., Su, L., Marslen-Wilson, W., & Kriegeskorte, N. (2014). A toolbox for representational similarity analysis. PLoS computational biology, 10(4), e1003553.

Sucholutsky, I., Muttenthaler, L., Weller, A., Peng, A., Bobu, A., Kim, B., ... & Griffiths, T. L. (2023). Getting aligned on representational alignment. arXiv preprint arXiv:2310.13018.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #3:

Comments on revised version:

This revised version is in large improved and the responses to reviewers' comments are generally relevant. However, the response regarding pre-nodes is not satisfactory. I understand that the authors prefer to avoid further experimentations, but I think this is an important point that needs to be clarified. Exploring stages between E12 and E15 are therefore of importance. When carefully examining some of the figures (Fig. 1E or 2D) I think that at E15 they may well be pre-nodes formation prior to myelin deposition, on structure the authors considered to be heminodes. To be convincing they should use double or triple labeling with, in addition to the nodal proteins (ankG and/or Nav pan), a good myelin marker such as antiPLP. The rat monoclonal developed by late Pr Ikenaka would give a sharper staining than the anti MAG they used. (I assume the clone must still be available in Okazaki ).

We appreciate your insightful comment regarding the possible presence of pre-nodal clusters along NM axons and your kind suggestion to use the PLP antibody (clone AA3; Yamamura et al., J Neurochem, 1991). We have obtained this monoclonal antibody from Dr. Kenji Tanaka previously in Okazaki and confirmed that it works well in chicken tissues. However, since this clone recognizes both PLP and DM-20 isoforms, it labels not only myelin-forming oligodendrocytes (MFOLs) but also newly formed oligodendrocytes (NFOLs) (Yokoyama et al., J Neurochem, 2025). Therefore, it is not ideal for determining whether nodal protein clusters are formed before myelin deposition.

Instead, we performed double immunostaining for MAG and AnkG between E12 and E15 to clarify the temporal relationship between myelin maturation and node formation. The results showed that detectable AnkG clusters along NM axons began to appear very sparsely around E13, coinciding with the emergence of MAG signals, and became more prominent with development. This temporal pattern does not match the definition of pre-nodal clusters, which are formed prior to myelination.

Although we cannot completely rule out the possibility of undetectable pre-nodal clusters or those composed of molecules other than AnkG, our results support the view that pre-nodal clusters are unlikely to play a major role in determining the regional difference in nodal spacing along NM axons. These new data have been added as Figure 2—figure supplement 1, and the relevant sections in the Results, Discussion, and Figure legend have been revised accordingly (page 5, line 4; page 10, line 7; page 29, line 1).

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

Summary:

The authors attempted to clarify the impact of N protein mutations on ribonucleoprotein (RNP) assembly and stability using analytical ultracentrifugation (AUC) and mass photometry (MP). These complementary approaches provide a more comprehensive understanding of the underlying processes. Both SV-AUC and MP results consistently showed enhanced RNP assembly and stability due to N protein mutations.

The overall research design appears well planned, and the experiments were carefully executed.

Strengths:

SV-AUC, performed at higher concentrations (3 µM), captured the hydrodynamic properties of bulk assembled complexes, while MP provided crucial information on dissociation rates and complex lifetimes at nanomolar concentrations. Together, the methods offered detailed insights into association states and dissociation kinetics across a broad concentration range. This represents a thorough application of solution physicochemistry.

We thank the Reviewer for this positive assessment. 

Weaknesses:

Unlike AUC, MP observes only a part of the solution. In MP, bound molecules are accumulated on the glass surface (not dissociated), thus the concentration in solution should change as time develops. How does such concentration change impact the result shown here?

We agree with the Reviewer that the concentration in solution above the surface will change with time; however, the impact of surface adsorption turns out to be negligible. To show this we have added a calculation as Supplementary Methods that is based on the number of imaged adsorption events, the fraction of imaged area to total surface area, and the initial sample volume and concentration. Under our experimental conditions the reduction is less than 1%, which is well within the range of experimental concentration errors.

This is in line with the observation that surface adsorption of proteins to glass is critical and needs to be prevented when working at picomolar concentrations (Zhao H, Mayer ML, Schuck P. 2014. Analysis of protein interactions with picomolar binding affinity by fluorescence-detected sedimentation velocity. Anal Chem 86:3181–3187. doi:10.1021/ac500093m), but is ordinarily negligible when working at the mid nanomolar concentration range. The difference in the MP experiments is that where usually the surface adsorption to glass and plastic is invisible, it is being imaged and quantified in MP. The negligible impact of surface adsorption on solution concentration in typical MP experiments is also in line with the results of several studies that have successfully measured dissociation constants of binding equilibria by MP (Young G et al., Science 360 (2018) 432; Wu & Piszczeck, Anal Biochem 592 (2020) 113575; Solterman et al. Angewandte Chemie 59 (2020) 10774) with samples in the 5-50 nM range and similar experimental setup. It should be noted that in the MP experiments no surface functionalization is employed, in contrast to optical biosensors that utilize surface-immobilized ligands and polymeric matrices and thereby enhance the surface binding capacity.

Even though this depletion effect is negligible under ordinary MP conditions, the Reviewer raises a good point and readers may have a similar question with this novel technique. For this reason, we have added in the MP section of the Methods the sentence “In either configuration, the impact of surface binding on the sample concentration is < 1% and negligible, as described in the Supplementary Methods S1.” and added the detailed calculations in the Supplement accordingly. The use of SV as a traditional, orthogonal technique and the observation of consistent results with those of MP should further dispel readers’ methodological concerns in this point.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors apply a variety of biophysical and computational techniques to characterize the effects of mutations in the SARS-CoV-2 N protein on the formation of ribonucleoprotein particles (RNPs). They find convergent evolution in multiple repeated independent mutations strengthening binding interfaces, compensating for other mutations that reduce RNP stability but which enhance viral replication.

Strengths:

The authors assay the effects of a variety of mutations found in SARS-CoV-2 variants of concern using a variety of approaches, including biophysical characterization of assembly properties of RNPs, combined with computational prediction of the effects of mutations on molecular structures and interactions. The findings of the paper contribute to our increasing understanding of the principles driving viral self-assembly, and increase the foundation for potential future design of therapeutics such as assembly inhibitors.

Thank you for highlighting the strengths of our paper and the potential impact on future design of therapeutics.

Weaknesses:

For the most part, the paper is well-written, the data presented support the claims made, and the arguments are easy to follow. However, I believe that parts of the presentation could be substantially improved. I found portions of the text to be overly long and verbose and likely could be substantially edited; the use of acronyms and initialisms is pervasive, making parts of the exposition laborious to follow; and portions of the figures are too small and difficult to read/understand.

We are glad the Reviewer concurs the data support our conclusions, and finds the arguments easy to follow.  We appreciate the comment that the work was not optimally presented. To address this point, we have identified multiple opportunities to streamline the text without jeopardizing the clarity. We have also rewritten the end of the Introduction.

As recommended, we have reduced and harmonized the use of acronyms and abbreviations throughout the text to improve readability. Specifically, we have now spelled out nucleic acid (NA), intrinsically disordered regions (IDR), full-length (FL), AlphaFold (AF3), and variants of concern (VOC).

Finally, we have improved the presentation of most figures, adding labels and new panels, and increased the label font sizes to facilitate more detailed inspections of the data.

Reviewer #3 (Public Review):

This manuscript investigates how mutations in the SARS-CoV-2 nucleocapsid protein (N) alter ribonucleoprotein (RNP) assembly, stability, and viral fitness. The authors focus on mutations such as P13L, G214C, and G215C, combining biophysical assays (SV-AUC, mass photometry, CD spectroscopy, EM), VLP formation, and reverse genetics. They propose that SARS-CoV-2 exploits "fuzzy complex" principles, where distributed weak interfaces in disordered regions allow both stability and plasticity, with measurable consequences for viral replication.

Strengths:

(1) The paper demonstrates a comprehensive integration of structural biophysics, peptide/protein assays, VLP systems, and reverse genetics.

(2) Identification of both de novo (P13L) and stabilizing (G214C/G215C) interfaces provides a mechanistic insight into RNP formation.

(3) Strong application of the "fuzzy complex" framework to viral assembly, showing how weak/disordered interactions support evolvability, is a significant conceptual advance in viral capsid assembly.

(4) Overall, the study provides a mechanistic context for mutations that have arisen in major SARS-CoV-2 variants (Omicron, Delta, Lambda) and a mechanistic basis for how mutations influence phenotype via altered biomolecular interactions.

We are grateful for these comments highlighting this work as a significant conceptual advance.

Weaknesses:

(1) The arrangement of N dimers around LRS helices is presented in Figure 1C, but the text concedes that "the arrangement sketched in Figure 1C is not unique" (lines 144-146) and that AF3 modeling attempts yielded "only inconsistent results" (line 149).

The authors should therefore present the models more cautiously as hypotheses instead. Additional alternative arrangements should be included in the Supplementary Information, so the readers do not over-interpret a single schematic model.

We agree that in the absence of high-resolution structures the RNP models are hypothetical, and have now emphasized this in the Results, following the Reviewer’s recommendation. To present alternative arrangements that satisfy the biophysical constraints upfront, we have promoted the previous Supplementary Figure 11 showing different models to the first Supplementary Figure, and expanded it with examples of different oligomers. In this way it is referenced early on in the Results and in the legend to Figure 1C. We agree this strengthens the manuscript, as one of the take-home messages is the inherent polydispersity of the RNPs.

The fact that AF3 can only provide inconsistent results will not come as a surprise, given the substantial disordered regions of the complex, and is a drawback of AF3 rather than our structural model. We slightly emphasized this point so as to clarify that the presentation of the AF3-based RNP structure serves solely as supporting evidence that our hypothetical model is sterically reasonable.

The new Results paragraph reads:

“As suggested in the cartoon of Figure 1C, this supports the hypothesis of a three-dimensional arrangement with a central LRS oligomer with symmetry properties and dimensions similar to low resolution EM images of model RNPs (Carlson et al., 2022, 2020) and cryo-ET of RNPs in virions (Klein et al., 2020; Yao et al., 2020).  It should be noted, however, that the arrangement sketched in Figure 1C is not unique and other subunit orientations could be envisioned that satisfy all constraints from experimentally observed binding interfaces, including different oligomers and anti-parallel subunits as illustrated in Supplementary Figure S1. Extending previous ColabFold structural predictions that show multiple N-protein dimers self-assembled via the LRS coiled-coils (Zhao et al., 2023), we attempted the AlphaFold modeling of RNPs combining multiple N dimers with SL7 RNA ligands, mimicking our biophysical assembly model. Current AlphaFold restrictions limit the prediction to pentamers of N-protein dimers with 10 copies of SL7 RNA. While only inconsistent results were obtained – which is not surprising given the large intrinsically disordered regions exceed the predictive power of AlphaFold – some models did produce an overall RNP organization similar to Figure 1C, suggesting such an arrangement is at least sterically reasonable with regard to possible N-protein subunit orientations in an RNP (Supplementary Figure S2)”

(2) Negative-stained EM fibrils (Figure 2A) and CD spectra (Figure 2B) are presented to argue that P13L promotes β-sheet self-association. However, the claim could benefit from more orthogonal validation of β-sheet self-association. Additional confirmation via FTIR spectra or ThT fluorescence could be used to further distinguish structured β-sheets from amorphous aggregation.

We completely agree that the application of multiple orthogonal biophysical methods can strengthen the conclusions. In addition to EM fibrils and CD spectra (a classical gold standard technique for protein secondary structure in solution), we already have support from ColabFold modeling, as well as NMR results from the Zweckstetter lab showing the potential for for β-sheet-like conformations.

Furthermore, we believe the evidence for the absence of ‘amorphous aggregates’ is very strong, as this would be inconsistent with the long-range order required to create the visibly fibrillar morphology in EM, and amorphous aggregates would be inconsistent with the increased solution viscosity. In this context, it is also highly relevant that the β-sheet-like secondary structure recorded by CD is concentration-dependent and reversible upon dilution. The long-range spatial order of fibrils is consistent with the formation of secondary structure in solution.

In addition, it must be kept in mind that what we see is specific to N-arm peptides carrying the P13L mutation (in EM, CD, and structural prediction) and does not occur in the other two N-arm peptides (ancestral N-arm and N-arm with deletion of 31-33), linker peptides, or C-arm peptides.

Most importantly, as elaborated in more detail below, we do not claim that fibril formation is physiologically relevant. At the heart of this – in the context of the evolution of fuzzy complexes – is that the P13L mutation creates additional weak protein-protein interactions. Indeed, the assembly of fibrils geometrically requires at least two interfaces for each subunit. These weak interactions are at play physiologically in the context of the disordered RNP particles, and in macromolecular condensates, but not in the formation of fibrils. Therefore, while we appreciate the suggestion for FTIR spectra ThT staining, we are afraid further emphasis on the fibril structure might confuse the reader, and therefore we would rather clarify upfront that these fibrillar assemblies are not thought to form in vivo from full-length protein, but merely demonstrate the presence of N-arm self-association interfaces in the model of truncated peptides.

Accordingly, we have amended the Results paragraph reporting the fibrils:

“Thus, the N-arm mutation P13L is responsible for the formation of fibrils in N-arm peptides after prolonged storage. Some of these N-arm fibrils exhibit a twisted morphology with width of »5 nm (Figure 2A), in some instances exhibiting patterns of strand breaks. Such fibrils are frequently encountered in proteins that can stack β-sheets, such as in amyloids (Paravastu et al., 2008). While we have not observed fibril formation in the context of full-length N, and have no evidence such fibrils are physiologically relevant, their occurrence in solutions of truncated N-arm peptide nonetheless demonstrates the introduction of ordered N-arm self-association interfaces in conformations of P13L mutants.”

And more completely summarized experimental evidence prior to describing the ColabFold prediction results (which previously did not include mention of the NMR):

“Finally, confirming the interpretation of the EM images and the CD data, as well as the b-structure propensity reported from NMR data (Zachrdla et al., 2022), the structural prediction of N[10-20]:P13L in ColabFold displayed oligomers with stacking b-sheets …”

(3) In the main text, the authors alternate between emphasizing non-covalent effects ("a major effect of the cysteines already arises in reduced conditions without any covalent bonds," line 576) and highlighting "oxidized tetrameric N-proteins of N:G214C and N:G215C can be incorporated into RNPs". Therefore, the biological relevance of disulfide redox chemistry in viral assembly in vivo remains unclear. Discussing cellular redox plausibility and whether the authors' oxidizing conditions are meant as a mechanistic stress test rather than physiological mimicry could improve the interpretation of these results.

The paper could benefit if the authors provide a summary figure or table contrasting reduced vs. oxidized conditions for G214C/G215C mutants (self-association, oligomerization state, RNP stability). Explicitly discuss whether disulfides are likely to form in infected cells.

We thank the Reviewer for raising this most interesting point.  The reason why the biological relevance of N dilsulfides remains unclear is simply that this is still unknown, unfortunately. Recently, Kubinski et al. have strongly argued for the formation of disulfides in infected cells, but in our view the evidence remains weak since the majority of disulfide bonds in that work presented as post-lysis artifacts, and it appears the non-covalent effects alone could explain the physiological observations. We aimed for a balanced presentation and wrote in the relevant Results section:

“Covalent disulfide bonds in the LRS in non-reducing conditions were found to further promote LRS oligomerization. However, there is no conclusive data yet whether covalent bonds in the LRS occur in vivo, or any G215C effect is entirely non-covalent due to the significant strengthening of LRS helix oligomerization (see Discussion).”

Despite the uncertainty regarding physiological disulfide bond formation, we believe it is useful to ask whether covalently crosslinked N dimers would aid or constrain RNP assembly in our biophysical model. We have now better explained this motivation in the Results section describing the RNP experiments:

“Even though it is still unclear whether disulfide bonds of N cysteine mutants form in vivo, we were curious about the impact of disulfide-linked oligomers of the cysteine mutants on their RNP structure and stability in our biophysical assembly model.”

The referenced paragraph from the Discussion reads:

“Regarding the cysteine mutations that have been repeatedly introduced in the LRS prior to the rise of the Omicron VOCs, it is an open question whether they lead to covalent bonds in vivo or in the VLP assay. While examples of disulfide-linked viral nucleocapsid proteins have been reported (Kubinski et al., 2024; Prokudina et al., 2004; Wootton and Yoo, 2003), a methodological difficulty in their detection is artifactual disulfide bond formation post-lysis of infected cells (Kubinski et al., 2024; Wootton and Yoo, 2003).  However, our results clearly show that a major effect of the cysteines already arises in reduced conditions without any covalent bonds, through extension of the LRS helices, and concomitant redirection of the disordered N-terminal sequence. While oxidized tetrameric N-proteins of N:G214C and N:G215C can be incorporated into RNPs, the covalent bonds provided only marginally improved RNP stability.  Interestingly, the introduction of cysteines imposes preferences of RNP oligomeric states dependent on oxidation state, consistent with our MD simulations highlighting the impact of cysteine orientation of 214C versus 215C relative to the hydrophobic surface of the LRS helices. Overall, considering potentially detrimental structural constraints from covalent bonds on LRS clusters seeding RNPs, energetic penalties on RNP disassembly, as well as the required monomeric state of the LRS helix for interaction with the NSP3 Ubl domain (Bessa et al., 2022), at present it is unclear to what extent the formation of disulfide linkages between LRS helices would be beneficial or detrimental in the viral life cycle.”

We feel that this text addresses the Reviewer’s comment, and that expanding the existing discussion further would conflict with other recommendations to shorten and focus the text.

Finally, we have addressed the valuable suggestion of a new table summarizing the oligomeric state and self-association of the different cysteine mutants by inserting a new column in the existing Table 1 reporting all species’ oligomeric state at low micromolar concentrations. In this way they can be compared at a glance with the other mutants as well. A more detailed comparison of the concentration-dependent size-distribution is provided in Figure 4.

(4) VLP assays (Figure 7) show little enhancement for P13L or G215C alone, whereas Figure 8 shows that P13L provides clear fitness advantages. This discrepancy is acknowledged but not reconciled with any mechanistic or systematic rationale. The authors should consider emphasizing the limitations of VLP assays and the sources of the discrepancy with respect to Figure 8.

We thank the Reviewer for this comment, which highlights a very important point. 

For clarification and to improve the cohesion of the manuscript we have inserted a reference to the Discussion after the presentation of the VLP results, which provides a natural transition to the following description of the reverse genetics experiments:

“As expanded on in the Discussion, the failure to observe enhancement by P13L alone may be related to limitations of the VLP assay in sensitivity, including the restriction to a single round of infection, and protein expression levels.”

This references a paragraph in the Discussion about the limitations of the VLP assay in general and the reasons we believe the enhancement by P13L alone was not picked up:

“…While this assay has been widely used for rapid assessment of spike protein and N variants (Syed et al., 2021), it has limitations due to the addition of non-genomic RNA and the lack of double membrane vesicles from which gRNA emerges through the NSP3/NSP4 pore complex potentially poised for packaging (Bessa et al., 2022; Ke et al., 2024; Ni et al., 2023). It should also be recognized that the results do not directly reflect the relative efficiency of RNP assembly only, since protein expression levels, their localization, and their posttranslational modifications are not controlled for. Susceptibility for such factors might be exacerbated with mutations that modulate weak protein interactions. For example, as shown previously (Syed et al., 2024; Zhao et al., 2024), a GSK3 inhibitor inhibiting N-protein phosphorylation significantly enhances VLP formation and eliminates the advantage provided for by the N:G215C mutation relative to the ancestral N – presumably due to an increase in assembly-competent, non-phosphorylated N-protein erasing an affinity advantage. A similar process may be underlying the absent or marginal improvement in VLP readout from the cysteine LRS mutants and P13L at the achieved transfection level in the present work, and the enhanced signal from R203K/G204R and R203M (the latter being consistent with previous reports (Li et al., 2025; Syed et al., 2021)) modulating protein phosphorylation. Nonetheless, mirroring the results of the biophysical in vitro experiments, the addition of RNP-stabilizing P13L and G214C mutations on top of R203K/G204R led to a significantly larger VLP signal.

The VLP assay may be limited in sensitivity to mutation effects due to its restriction to a single round of infection. To avoid this and other potential limitations of the VLP assay for the study of viral packaging, for the key mutation N:P13L we carried out reverse genetics experiments. These showed the sole N:P13L mutation significantly increases viral fitness (Figure 8).”

(5) Figures 5 and 6 are dense, and the several overlays make it hard to read. The authors should consider picking the most extreme results to make a point in the main Figure 5 and move the other overlays to the Supplementary. Additionally, annotating MP peaks directly with "2×, 4×, 6× subunits" can help non-experts.

We completely agree with the Reviewer – these figures were very dense.  To mitigate this problem without having the reader to switch back-and-forth to the supplement, we subdivided the panels of Figure 5 and showed only a subset of curves in each.  In this way the data are easier to read while still readily compared. It is a large figure, but it contains the key data for the present work and is therefore worthwhile to have in one place. For the MP histogram data we also have inserted the suggested peak labels. Similarly, we have split Figure 6A into two panels for clarity.

(6) The paper has several names and shorthand notations for the mutants, making it hard to keep up. The authors could include a table that contains mutation keys, with each shorthand (Ancestral, Nο/No, Nλ, etc.) mapped onto exact N mutations (P13L, Δ31-33, R203K/G204R, G214C/G215C, etc.). They could then use the same glyphs (Latin vs Greek) consistently in text and figure labels.

Yes, we agree this is a problem and we apologize for the confusion. However, it is not possible to refer exclusively to either Latin or Greek terminology, which we feel would be even more detrimental to readability (the former being exhaustively lengthy and the latter being imprecise). But we have used a rational system: If the complete set of mutations of a variant are present, then its Greek letter will be used as an abbreviation, and otherwise we use Latin amino acid/position indicators for individual mutations or combinations thereof. Unfortunately, previously we inadvertently failed to explicitly mention this, and we are most grateful for the Reviewer to point this out.

We have now rectified this by including upfront the sentence:

“We will adopt a nomenclature where the complete set of defining mutations of a variant will be referred to by its Greek letter, i.e., N:P13L/R203K/G204R/G214C is N_­­λ, and analogously the set of Omicron mutations N:P13L/Δ31-33/R203K/G204R are referred to as N_ο; see Table 1”

This will define the two shorthands N_λ and N_ο used. Furthermore, as suggested and pointed to in the text, Table 1 does provide the keys to mutation and variants, including the information in which variant any of the other mutations studied here occur.

(7) The EM fibrils (Figure 2A) and CD spectra (Figure 2B) were collected at mM peptide concentrations. These are far above physiological levels and may encourage non-specific aggregation. Similarly, the authors mention" ultra-weak binding energies that require mM concentrations to significantly populate oligomers". On the other hand, the experiments with full-length protein were performed at concentrations closer to biologically relevant concentrations in the micromolar range. While I appreciate the need to work at high concentrations to detect weak interactions, this raises questions about physiological relevance.

This is indeed an important point to clarify. We agree that much lower nucleocapsid protein concentrations are present in the cytosol on average, and these were used in our RNP assembly experiments. However, there are at least two important physiologically relevant cases where high local N concentrations do occur:

(1) Once assembled in RNPs, the disordered N-terminal extensions are locally at a very high concentration within the volume they can explore while tethered to the NTD. A back-of-the-envelope calculation assuming 12 N-protein subunits confining 12 N-terminal extensions to the volume of a single RNP (≈14x14x14 nm³ by cryoEM; Klein et al 2020) leads to an effective concentration of 7.4 mM. Obviously the N-arm peptides are not completely free and there will be constraints that would hinder or promote encounter complex probability, but interfaces with mM Kd are clearly strong enough to populate Narm-Narm contacts extending from N-protein in the RNP.

Additionally, any interaction where N-proteins are brought in close proximity could allow weak N-arm interactions to provide additional stability. Besides the RNP, we demonstrate this in our Results for nucleic-acid liganded N tetramers (Figure 4B), but this might similarly occur in complexes with NSP3 or host proteins. Generally, it is quite common that small additional binding energies play important roles in the modulation of multivalent protein complexes.

(2) Within the macromolecular condensate the local concentration will be substantially higher than on average within the infected cell.  While we do not know its precise concentration, it is well-established that the sum of many ultra-weak interactions is driving the formation of this dense liquid phase. In our previous eLife paper (Nguyen et al., 2024) we have shown LLPS is suppressed with the R203K/G204R mutation, but it is ‘rescued’ with the additional P13L/del31-33 mutation of the Omicron variant showing strong LLPS. Similarly, LLPS is suppressed by the LRS mutant L222P, but rescued in conjunction with P13L. This is another biologically relevant scenario where weak interactions are critical.

We have emphasized these points in the revised manuscript as described below.

Specifically:

(a) Could some of the fibril/β-sheet features attributed to P13L (Figure 2A-C) reflect non-specific aggregation at high concentrations rather than bona fide self-association motifs that could play out in biologically relevant scenarios?

We understand this concern from the experience with proteins that often have limited solubility and tendencies to aggregate, sometimes accompanied by unfolding and driven by hydrophobic interactions, or clustering on the path to LLPS. However, we are struggling to reconcile the picture of non-specific aggregation with the context of our P13L N-arm peptides. The term ‘non-specific aggregation’ implies the idea of amorphous aggregates, which we would contend is inconsistent with the observed geometry of fibrils, which exhibit long-range order. In addition, non-specific aggregation does not lead to increased solution viscosity, which we describe, but fibril formation does. Another connotation of ‘aggregates’ is irreversibility.  However, we find the beta-sheet-like conformation seen at 1 mM becomes significantly more disordered when the same sample is diluted to 0.4 mM peptide. This is consistent with a reversible self-association driven by a conformational change toward ordered secondary structure.

To highlight the reversibility, we have clarified the description: “Interestingly, diluting the 1 mM sample (solid) to a concentration of 0.4 mM (dashed) reveals a large shift in the far-UV spectra … both indicative of a significant increase of disorder upon dilution. This is consistent with the stabilization of b-sheets in a reversible, strongly cooperative self-association process with an effective K_D in the high mM to low mM range.”

We have also inserted a concentration conversion to mg/ml units, which shows even 1 mM of peptides is only ~5 mg/ml, i.e. not excessively high. “While the ancestral N-arm at »1 mM (» 4.6 mg/ml) concentrations exhibits CD spectra with a minimum at »200 nm typical of disordered conformations (black)”

With regard to the question of specificity, we have studied similar N-arm peptides without P13L mutations and with the 31-33 deletion under equivalent conditions. But we observe the reversible self-association, conformational change, and fibril formation only for those containing the P13L mutation, consistent with ColabFold predictions. Neither did we observe fibrils with disordered C-arm peptides.

How these weak self-association motifs in the N-arm can be physiologically relevant in the context of full-length protein modulating the stability of multi-molecular complexes and enhancing LLPS was outlined above, and further clarified in the manuscript as detailed below.

(b) How do the authors justify extrapolating from the mM-range peptide behaviors to the crowded but far lower effective concentrations in cells?

As pointed out above, the key to this question is the local preconcentration as the N-arm peptides are tethered to the rest of protein in the context of flexible multi-molecular assemblies. Another mechanism to consider is the formation of condensates. The response to the next comment will expand on this.

The authors should consider adding a dedicated section (either in Methods or Discussion) justifying the use of high concentrations, with estimation of local concentrations in RNPs and how they compare to the in vitro ranges used here. For concentration-dependent phenomena discussed here, it is vital to ensure that the findings are not artefacts of non-physiological peptide aggregation..

The use of high concentration in biophysical experiments is quite common, for example, in NMR or crystallography, insofar as they elucidate molecular properties. We believe this is obvious; the Reviewer will certainly agree with us, and this does not require further elaboration. The property observed in this case is the existence of specific, weak protein self-association interfaces in the N-arm.

Our response to the Reviewer’s point 7(a) addresses the distinction between artefactual aggregation and self-association of N-arm peptides. The relevance of these weak protein self-association interfaces in the context of the full-length protein is the second underlying question.

As we have previously stated in a dedicated Results paragraph:

“In contrast to the modulation of the coiled-coil LRS interfaces, the de novo creation of the N-arm self-association interface through beta-sheet interactions enabled by P13L cannot be readily observed in full-length N-protein at low M concentrations. Similar to the ancestral LRS interface, it provides only ultra-weak binding energies that require mM concentrations to significantly populate oligomers. This is fully consistent with the previous observation by SV-AUC that neither N:P13L,31-33 nor N_o with the full set of Omicron mutations show any significant higher-order self-association at low M concentrations, whereas at high local concentrations – as observed in phase-separated droplets – they can modulate and cooperatively enhance self-association processes (Nguyen et al., 2024). (If fact, P13L can substitute for the LRS promoting LLPS, as observed in the rescue of LLPS by N:P13L,31-33/L222P mutants whereas N:L222P LRS-abrogating mutants are deficient in LLPS.) Another process that increases the local concentration of N-arm chains is the tetramerization of full-length N-protein. As described earlier, occupancy of the NA-binding site in the NTD allosterically promotes self-assembly of the LRS into higher oligomers (Zhao et al., 2021). We hypothesized that these oligomers may be cooperatively stabilized by additional N-arm interactions in P13L mutants.”

To state completely unambiguously why weak interfaces are important, we have followed the Reviewer’s suggestion and added an additional clarification already earlier, at the end of the P13L Results section:

“While this self-association interface in the P13L N-arm is weak and its direct observation in biophysical experiments requires mM concentrations, which far exceed average intracellular concentration of N, such  weak interactions can become highly relevant physiologically when high local concentrations are prevailing, for example, when the disordered extension is preconcentrated while tethered within macromolecular assemblies as in the RNP, or in macromolecular condensates.”

Furthermore, we have added early in the Discussion:

“Even though the solution affinity of the N-arm P13L interface is ultra-weak, the average local concentration of N-arm chains across the RNP volume (in a back-of-the-envelope calculation assuming a ≈14 nm cube (Klein et al., 2020) with a dodecameric N cluster) is ≈7.4 mM, such that disordered N-arm peptides could well create populations of N-arm clusters stabilizing RNPs through this interface.  However, besides the RNP-stabilizing mutants we have also observed unexpected RNP destabilization by the ubiquitous R203K/G204R double mutation, which may be caused by the introduction of additional charges close to the self-association interface in the LRS. In our experiments, this destabilization is more than compensated for by the P13L mutation. (Another scenario where ultra-weak interactions can have a critical impact is in molecular condensates. We previously reported the suppression of LLPS by the R203K/G204R mutation, which is rescued by the additional P13L/Δ31-33 mutation (Nguyen et al., 2024). This is consistent with compensatory weak stabilizing and destabilizing impacts of weak interactions on the RNP observed here.)”

Reviewer #1 (Recommendations for the Authors):

In Figure 1B, it is unclear what the orange lines connecting polypeptides represent, as well as the zig-zag orange lines in the N-arm.

We thank the Reviewer for this comment. We intended this to represent regions of self-association but recognize the patterned background is confusing. We have changed this now to solid-colored backgrounds, and indicated this in the figure legend:

“Regions of self-association are indicated by shaded backgrounds.”

Regarding presentation, in Figure 5 (MP), the relationship between mass and oligomer size should be shown more clearly.

We agree. To this end we have labeled the peaks in the MP histograms in Figure 5 with the oligomeric state of the 2N/2SL7 subunits.

Reviewer #2 (Recommendations for the Authors):

I find the science of the paper to be convincing and compellingly supported.

Thank you for this positive statement.

My primary complaints are with presentation or minor technical questions that, honestly, primarily arise due to my own ignorance and unfamiliarity with some of the techniques employed.

My primary issue is with the figures. I find, generally, the text in axes labels, ticks, and legends to be too small to comfortably read. This is particularly true in the CD spectra and

other data presented in Figures 1D, 2B, 4, 5, 6, and 8.

We agree and have increased the font size of all text and labels of the plots in Figure 1, 2, 4, 5, 6, and 8.

I also found the use of initialisms to be a bit overbearing and inconsistent. For example, the authors repeatedly switch between spelling out "nucleic acid" and the initialism "NA" (which is also never explicitly spelled out in the text). With the already substantial length of the text, my own personal opinion would be to suggest spelling out all initialisms in the interest of making the reading easier.

This is a valid criticism. To improve the readability, we have followed this advice and systematically spelled out “nucleic acid” instead of using “NA”.  Similarly, we have now written out full-length instead of the abbreviation FL, and omitted the abbreviation IDR for intrinsically disordered regions, as well as VOC for variant of concern, and AF3 for AlphaFold.

Regarding the reference to mutants, we have now explained upfront the system of Latin and Greek nomenclature we consistently applied.

“We will adopt a nomenclature where the complete set of defining mutations of a variant will be referred to by its Greek letter, i.e., N:P13L/R203K/G204R/G214C is N­­_l, and analogously the set of Omicron mutations N:P13L/Δ31-33/R203K/G204R are referred to as N_ο; see Table 1”

I found the text to be verbose, bordering on overly so; the Introduction is more than two pages long. The section "Enhanced oligomerization of the leucine-rich sequence through cysteine mutations" has two long paragraphs of introduction before the present results are discussed, et cetera. An (admittedly, very rough) estimation of the length of the paper places it at ~9,000 -10,000 words long, and I think that the presentation might benefit from significant editing and

shortening.

We agree the manuscript is longer than would be desirable, and we generally prefer not to insert mini-introductions into Results sections. On the other hand, in order to make a solid contribution to understanding the big picture of fuzzy complexes in molecular evolution of RNA virus proteins it is indispensable to go into the details of RNP assembly and several of the interfaces. Therefore, we feel the length is in the range that it needs to be without losing clarity. In addition, other Reviewer suggestions to extend the discussion, for example, of limitations of VLP assays and the in vivo state of cysteines, conflict with significant shortening.

In the particular case of the cysteine mutations, cited by the Reviewer, we believe it is important to add detailed background on G215C, because the Results proceed in a comparison of the self-association mode between G215C and G214C. This is of significant interest in the present context not only for the independent introduction of interface-enhancing mutations highlighting the evolution of fuzzy complexes, but also because it illustrates the pleomorphic ability of RNPs.

Nonetheless, we have slightly shortened this text and merged the background into a single paragraph. More generally, we have critically reread the text to remove tangential sentences where possible and to make it more concise.

I have a few more specific comments.

In Figure 1A, I suggest explicitly labeling the location of the LRS, as it comes up repeatedly.

Yes, we thank the Reviewer for this suggestion and have introduced this label in Figure 1A.

In Figure 1B, the legend indicates that the red lines indicate "new inter-dimer interactions." However, these red lines are overlayed on a vertical stripe of red squiggles; it is unclear to me and not explicitly described in the legend what these squiggles are meant to illustrate.

We agree this background was confusing. As mentioned in our Response to Reviewer #1 we have replaced the structured background with a solid background and explained in the figure legend that these areas depict regions of self-association.

On lines 44-45, the authors state, "The IDRs amount to 45%, ..." 45% of what?

Thank you, this was unclear.  We have now clarified “The IDRs amount to ≈45% of total residues”

In lines 244 - 246, the authors compare the sizes of complexes in reducing versus non- reducing conditions as measured by dynamic light scattering, stating, "However, dynamic light scattering (DLS) revealed the presence of N210-246:G214C complexes with hydrodynamic radii 244 ranging from 6 to 40 nm (in comparison to 1-2 nm for N210- 246:G215C(Zhao et al., 2022)) in reducing conditions, and slightly larger in non-reducing conditions (Supplementary Figure S4)." Using this single statistic seems to me to be a less-than-ideal way of characterizing what seems to me to be happening here. In Supplementary Figure 4, it appears to me that what is happening is that in non-reduced conditions, the sample is monodisperse, whereas in reducing conditions, the distribution becomes polydisperse/bimodal, with two clearly separate populations. I feel that this could use a more

thorough description rather than just stating the overall range of particle sizes.

Yes, the Reviewer is correct – it is indeed a good idea to be more precise here. To this end we have carried out cumulant analyses on the autocorrelation functions, as a time-honored method to quantify the polydispersity.  Both samples are polydisperse, but more so in reducing conditions. We have now added “For N210-246:G214C a cumulant analysis results in radii of 8.8 nm and 10.6 nm and polydispersity indices of 0.40 and 0.35 for reducing and non-reducing conditions, respectively”

Finally, I have one remaining comment that is a result of my own inexperience with circular dichroism and interpreting the spectra. For me personally, I would appreciate a more thoroughdescription/illustration of the statistics involved in the CD spectra, but perhaps this is not necessary for people who are more familiar with interpreting these kinds of data. For example, in Figure 1D, it is not clear to me what the error bars/confidence intervals for the CD data look like. I see many squiggles, some of which the authors claim are significant (e.g., the differences between ~215 - 230 nm), and others are not worthy of comment. Let's say, for example, that I fit a smoothed spline through these data and then measure the magnitude of the fluctuations from that spline to define/quantify confidence intervals. What does that distribution look like? Or maybe the confidence intervals are so small that all squiggles are significant?

Thank you, this is a good question. As mentioned in the methods section, the CD spectra shown are averages of triplicate scans. Therefore, it is straightforward to extract the standard deviation at each wavelength from the three measurements (although a spline would probably work just as well). The values are what one would expect for the squiggles to be random noise. In the region 215 – 220 nm characteristic for helical secondary structure the standard deviations are small relative to the separation between curves, which indicates that the differences are highly significant. Naturally, the curves do overlap in other spectral regions, which would make a plot including the wavelength-dependent error bars or confidence bands too crowded. Therefore, we have kept the plot of the averaged triplicate scans, but have now provided the average standard deviations for all species in the figure legend and mentioned their significant separation:

“Triplicate scans yield average standard deviations of 0.13 (N), 0.17 (N+SL7), 0.16 (N_l), and 0.21 (N_l +SL7) 10³ deg cm²/dmol, respectively, with non-overlapping confidence bands for the different species, for example, between 215-220 nm.”

Reviewer #3 (Recommendations for the Authors):

(1) The Discussion reiterates much of the background (mutational tolerance, fuzziness, SLiMs) already covered in the Introduction, diluting focus on the key new findings. The authors should consider shortening and refocusing the discussion on the main contributions in light of existing knowledge of viral assembly.

In the Introduction we have provided background on intrinsically disordered proteins in general and their mutational tolerance, as well as the concept of fuzzy complexes. The first several paragraphs of the Discussion have a different focus, which is protein binding interfaces between viral proteins (obviously key in fuzzy complexes), specifically their modulation and the remarkable de novo introduction of binding interfaces. We believe this deserves emphasis, since this highlights a novel aspect of fuzziness, for the mutant spectrum of RNA viruses to encode a range and of assembly stabilities and architectures. 

To reduce redundancy between the end of the Introduction and the beginning of the Discussion, we have shortened the last paragraph of the Introduction and removed its preview of the conclusions, as described in the response to the next comment of the Reviewer (see below).

Unfortunately, the length of the Discussion is dictated in part also by the need to discuss methodological aspects, among them the limitations of VLP assays, and the redox state of the cysteine in the LRS mutants, which were important points recommended by other suggestions of the Reviewers. Similarly, we believe the discussion of other potential functions of Omicron N-arm mutations is warranted, as well as the background of the R203K/G204R double mutation that has attracted significant attention in the field due to its effects on phosphorylation and expression of truncated N species that also form RNPs. Our goal was to integrate the results by us and other laboratories regarding specific mutation effects into a comprehensive picture of molecular evolution of N, which we believe the framework of fuzzy complexes can provide.

(2) The Abstract and early Introduction set a broad stage (IDPs, fuzziness), but don't explicitly state the concrete hypotheses that the experiments test. Please add 2-3 sentences in the Introduction that enumerate testable hypotheses, e.g.:

(a) P13L creates a new N-arm interface that increases RNP stability.

(b) G214C/G215C strengthens LRS oligomerization to stabilize higher-order N assemblies.

We agree the introduction can be improved.  However, it seems to us that it cannot be neatly framed in the hypothesis – answer dichotomy, without losing a lot of nuances and without requiring an even longer and more detailed introduction.

One of the main questions is to test whether the framework of fuzzy complexes can be applied to understand molecular evolution of N, and we feel the introduction is already flowing well towards this:

“ … In fuzzy complexes the total binding energy is distributed into multiple distinct ultra-weak interaction sites (Olsen et al., 2017). Similar to individual RNA virus proteins with loose or absent structure, maintaining disorder and a spatial distribution of low-energy interactions in the protein complexes may increase the tolerance for mutations and improve evolvability of protein complexes.\

The unprecedented worldwide sequencing effort of SARS-CoV-2 genomes during its rapid evolution in humans provides a unique opportunity to examine these concepts. ...”

To bring this to a more concrete set of questions in the end, we have shortened and rewritten the last paragraph in the Introduction:

“To examine how architecture and energetics of RNP assemblies can be impacted by N-protein mutations we study a panel of N-proteins derived from ancestral Wuhan-Hu-1 and different VOCs, including Alpha, Delta, Lambda, and Omicron (see Table 1), in biophysical experiments, VLP assays, and mutant virus. Specifically, we ask how the RNP size distribution and life-time is modulated by: (1) the novel binding interface created by the P13L mutation of Omicron; (2) enhancements of other weak self-association interfaces through G215C of Delta and G214C of Lambda; (3) the ubiquitous R203K/G204R double mutation of Alpha, Lambda, and Omicron.  We also test whether the P13L mutation improves viral fitness, similar to G215C and R203K/G204R. The results are discussed in the framework of fuzzy complexes and molecular evolution of N in the course of viral adaptation to the human host. Understanding the salient features of the binding interfaces in viral assembly and their evolution expands our foundation for the design of therapeutics such as assembly inhibitors.”

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):  

From my reading, this study aimed to achieve two things:  

(1) A neurally-informed account of how Pieron's and Fechner's laws can apply in concert at distinct processing levels.  

(2) A comprehensive map in time and space of all neural events intervening between stimulus and response in an immediately-reported perceptual decision.  

I believe that the authors achieved the first point, mainly owing to a clever contrast comparison paradigm, but with good help also from a new topographic parsing algorithm they created. With this, they found that the time intervening between an early initial sensory evoked potential and an "N2" type process associated with launching the decision process varies inversely with contrast according to Pieron's law. Meanwhile, the interval from that second event up to a neural event peaking just before response increases with contrast, fitting Fechner's law, and a very nice finding is that a diffusion model whose drift rates are scaled by Fechner's law, fit to RT, predicts the observed proportion of correct responses very well. These are all strengths of the study.   

We thank the reviewer for their comments that added context to the events we detected in relation to previous findings. We also believe that the change in the HMP algorithm suggested by the reviewer improved the precision of our analyses and the manuscript. We respond to the reviewer’s specific comments below.

(1) The second, generally stated aim above is, in the opinion of this reviewer, unconvincing and ill-defined. Presumably, the full sequence of neural events is massively task-dependent, and surely it is more in number than just three. Even the sensory evoked potential typically observed for average ERPs, even for passive viewing, would include a series of 3 or more components - C1, P1, N1, etc. So are some events being missed? Perhaps the authors are identifying key events that impressively demarcate Pieron- and Fechner-adherent sections of the RT, but they might want to temper the claim that they are finding ALL events. In addition, the propensity for topographic parsing algorithms to potentially lump together distinct processes that partially co-evolve should be acknowledged.  

We agree with the reviewer that the topographical solutions found by HMP will be dependent on the task and the quality and type of data. We address this point in the last section of the discussion (see also response to R3.5). We would also like to add that the events detected by HMP are, by construction, those that contribute to the RT and not necessarily all ERPs elicited by a stimulus.

In addition to the new last section of the discussion we also make these points clear in the revised manuscript at the discussion start: 

“By modeling the recorded single-trial EEG signal between stimulus onset and response as a sequence of multivariate events with varying by-trial peak times, we  aimed to detect recurrent events that contribute to the duration of the reaction time in the present perceptual decision-making task”.

Regarding the typical visual ERPs, in response to this comment but also comments R1.2, R1.3 and R2.1, we aimed for a more precise description of the topographies and thus reduced the width of the HMP expected events to 25ms. This ensures that we do not miss events shorter than the initial expectations of 50ms (see Appendix B of Weindel et al., 2024 and also response to  R1.3). This new estimation provides evidence for at least two of the visual ERPs that, based on their timings and topographies (in relation with the spatial frequency of the stimulus), we interpret as the N40 and the P100 (see response to R1.5 for the justification of this categorization). We provide a description and justification of the interpretations in the result section “Five trial-recurrent sequential events occur in the EEG during decisions” and the discussion section “Visual encoding time”.

(2) To take a salient example, the last neural event seems to blend the centroparietal positivity with a more frontal midline negativity, some of which would capture the CNV and some motor-execution related components that are more tightly time-locked to, of course, the response. If the authors plotted the traditional single-electrode ERP at the frontal focus and centroparietal focus separately, they are likely to see very different dynamics and contrast- and SAT-dependency. What does this mean for the validity of the multivariate method? If two or more components are being lumped into one neural event, wouldn't it mean that properties of one (e.g., frontal burstiness at response) are being misattributed to the other (centroparietal signal that also peaks but less sharply at response)?

Using the new HMP parameterization described above we show that the reviewer's intuition was correct. Using an expected pattern duration of 25ms the last event in the original manuscript splits in two events. The before-last event, now referred to the lateralized readiness potential (LRP) presents a strong lateralization (Figure 3) with an increased negativity over the motor cortex contralateral to the right hand. The effect of contrast is mostly on the last event that we interpret as the CPP (Figure 5). Despite the improved precision of the topographies of the identified events, it is however to be noted that some components will overlap. If the LRP is generated when a certain amount of evidence is accumulated (e.g. that the CPP crosses a certain value) then a time-based topography will necessarily include that CPP activity in addition to the lateralized potential. We discuss this in the section “Motor execution” of the discussion:

“Adding the abrupt onset of this potential, we believe that this event is the start of motor execution, engaged after a certain amount of evidence. The evidence for this interpretation is manifest in the fact that the event's topography shares some activity with the CPP event that follows, an expected result if the LRP is triggered at a certain amount of evidence, indexed by the CPP”.

(3) Also related to the method, why must the neural events all be 50 ms wide, and what happens if that is changed? Is it realistic that these neural events would be the same duration on every trial, even if their duration was a free parameter? This might be reasonable for sensory and motor components, but unlikely for cognitive.  

The HMP method is sensitive to the event's duration as shown in the manuscript about the method (Appendix B of Weindel et al., 2024). Nevertheless as long as the topography in the real data is longer than the expected one it shouldn't be missed (i.e. same goes for by-trial variations in the event width). For this reason we halved the expected event width of 50ms (introduced by the original HsMM-MVPA paper by Anderson and colleagues) in the revision. This new estimation with 25ms thus is much less likely to miss events as evidenced by the new visual and motor events. In the revised manuscript this is addressed at the start of the Results section:

“Contrary to previous applications (Anderson et al.,2016; Berberyan et al., 2021; Zhang et al., 2018; Krause et al., 2024) we assumed that the multivariate pattern was represented by a 25ms half-sine as our previous research showed that a shorter expected pattern width increases the likelihood of detecting cognitive events (see Appendix B of Weindel et al., 2024)”.

Regarding the event width as a free parameter this is both technically and statistically difficult to implement as the amount of computing capacity, flexibility and trade-offs among the HMP parameters would, given the current implementation, render the model unfit for most computers and statistically unidentifiable.

(4) In general, I wonder about the analytic advantage of the parsing method - the paradigm itself is so well-designed that the story may be clear from standard average event-related potential analysis, and this might sidestep the doubts around whether the algorithm is correctly parsing all neural events.  

Average ERP analysis suffers from an impossibility to differentiate between an effect of an experimental factor on the amplitude vs. on the timing of the underlying components (Luck, 2005). Furthermore the overlap of components across trials bluries the distinction between them. For both reasons we would not be able to reach the same level of certainty and precision using ERP analyses. Furthermore the relatively low number of trials per experimental cell (contrast level X SAT X participant = 6 trials) makes the analyses hard to perform on ERP which typically require more trials per modality. From the reviewer’s comment we understand that this point was not clear. We therefore discuss this in the revision, Section “Functional interpretation of the events” of the results:

“Nevertheless identifying neural dynamics on these ERPs centered on stimulus is complicated by the time variation of the underlying single-trial events (see probabilities displayed in Figure 3 for an illustration and Burle et al., 2008, for a discussion). The likely impact of contrast on both amplitude and time on the underlying single-trial event does not allow one to interpret the average ERP traces as showing an effect in one or the other dimension without strong assumptions (Luck, 2005)”.

(5) In particular, would the authors consider plotting CPP waveforms in the traditional way, across contrast levels? The elegant design is such that the C1 component (which has similar topography) will show up negative and early, giving way to the CPP, and these two components will show opposite amplitude variations (not just temporal intervals as is this paper's main focus), because the brighter the two gratings, the stronger the aggregate early sensory response but the weaker the decision evidence due to Fechner. I believe this would provide a simple, helpful corroborating analysis to back up the main functional interpretation in the paper.  

We agree with the suggestion and have introduced the representation on top of Figure 5 for sets of three electrodes in the occipital, posterior and frontal regions. The new panels clearly show an inversion of the contrast effect dependent on the time and locus of the electrodes. We discuss this in Section “Functional interpretation of the events” of the results:

“This representation shows that there is an inversion of the contrast effect with higher contrasts having a higher amplitude on the electrodes associated with visual potentials in the first couple of deciseconds (left panel of Figure 5A) while parietal and frontal electrodes shows a higher amplitude for lower contrasts in later portions of the ERPs (middle and right panel of Figure 5A)”.

To us, this crucially shows that we cannot achieve the same decomposition using traditional ERP analyses. In these plots it appears that while, as described by the reviewer, there is an inversion, the timing and amplitude of the changes due to contrast can hardly be interpreted.

(6) The first component is picking up on the C1 component (which is negative for these stimulus locations), not a "P100". Please consult any visual evoked potential study (e.g., Luck, Hillyard, etc). It is unexpected that this does not vary in latency with contrast - see, for example. Gebodh et al (2017, Brain Topography) - and there is little discussion of this. Could it be that nonlinear trends were not correctly tested for?  

We disagree with the reviewer on the interpretation of the ERP. The timing of the detected component is later than the one usually associated with a C1. Furthermore the central display does not create optimal conditions to detect a C1

We do agree that the topography raises the confusion but we believe that this is due to the spatial frequency of the stimulus that generates a high posterior positivity (see references in the following extract). The new HMP solution also now happens to show an effect of contrast on the P100 latencies, we believe this is due to the increased precision in the time location of the component. We discuss this in the “Visual encoding time” section of the discussion:

“The following event, the P100, is expressed around 70ms after the N40, its topography is congruent with reports for stimuli with low spatial frequencies as used in the current study (Kenemans et al., 2002, 2000; Proverbio et al., 1996). The timing of this P100 component is changed by the contrast of the stimulus in the direction expected by the Piéron law (Figure 4A)”. 

(7) There is very little analysis or discussion of the second stage linked to attention orientation - what would the role of attention orientation be in this task? Is it spatial attention directed to the higher contrast grating (and if so, should it lateralise accordingly?), or is it more of an alerting function the authors have in mind here?  

We agree that we were not specific enough on the interpretation of this attention stage. We now discuss our hypothesis in the section “Attention orientation” of the discussion:  

“We do however observe an asymmetry in the topographical map Figure 3. This asymmetry might point to an attentional bias with participants (or at least some participants) allocating attention to one side over the other in the same way as the N2pc component (Luck and Hillyard, 1994, Luck et al., 1997). Based on this collection of observations, we conclude that this third event represents an attention orientation process. In line with the finding of Philiastides et al. (2006), this attention orientation event might also relate to the allocation of resources. Other designs varying the expected cognitive load or spatial attention could help in further interpreting the functional role of this third event”.

We would like to add that it is unlikely that the asymmetry we mention in the discussion cannot stem from the redirection towards higher contrast as the experimental design balanced the side of presentation. We therefore believe that this is a behavioral bias rather than a bias toward the highest contrast stimulus as suggested by the reviewer. We hope that, while more could be tested and discussed, this discussion is sufficient given the current manuscript's goal.

Reviewer #2 (Public review):  

Summary:  

The authors decomposed response times into component processes and manipulated the duration of these processes in opposing directions by varying contrast, and overall by manipulating speed-accuracy tradeoffs. They identify different processes and their durations by identifying neural states in time and validate their functional significance by showing that their properties vary selectively as expected with the predicted effects of the contrast manipulation. They identify 3 processes: stimulus encoding, attention orienting, and decision. These map onto classical event-related potentials. The decision-making component matched the CPP, and its properties varied with contrast and predicted decision-accuracy, while also exhibiting a burst not characteristic of evidence accumulation.  

Strengths:  

The design of the experiment is remarkable and offers crucial insights. The analysis techniques are beyond state-of-the-art, and the analyses are well motivated and offer clear insights.  

Weaknesses:  

It is not clear to me that the results confirm that there are only 3 processes, since e.g., motor preparation and execution were not captured. While the authors discuss this, this is a clear weakness of the approach, as other components may also have been missed. It is also unclear to what extent topographies map onto processes, since, e.g., different combinations of sources can lead to the same scalp topography.  

We thank the reviewer for their kind words and for the attention they brought on the question of the missing motor preparation event. In light of this comment (and also R1.1, R3.3) the revised manuscript uses a finer grained approach for the multivariate event detection. This preciser estimation comes from the use of a shorter expected pattern in which the initial expectation of a 50ms half-sine was halved, therefore ensuring that we do not miss events shorter than the initial expectations (see Appendix B of Weindel et al., 2024 and also response to  R1.3). In the new solution the motor component that the reviewer expected is found as evidenced by the topography of the event, its lateralization and a time-to-response congruent with a response execution event. This is now described in the section “Motor execution” of the revised manuscript: 

“The before last event, identified as the LRP, shows a strong hemispheric asymmetry congruent with a right hand response. The peak of this event is approximately 100 ms before the response which is congruent with reports that the LRP peaks at the onset of electromyographical activity in the effector muscle (Burle et al., 2004), typically happening 100ms before the response in such decision-making tasks (Weindel et al., 2021). Furthermore, while its peak time is dependent on contrast, its expression in the EEG is less clearly related to the contrast manipulation than the following CPP event”.

Reviewer #3 (Public review):  

Summary:  

In this manuscript, the authors examine the processing stages involved in perceptual decision-making using a new approach to analysing EEG data, combined with a critical stimulus manipulation. This new EEG analysis method enables single-trial estimates of the timing and amplitude of transient changes in EEG time-series, recurrent across trials in a behavioural task. The authors find evidence for three events between stimulus onset and the response in a two-spatial-interval visual discrimination task. By analysing the timing and amplitude of these events in relation to behaviour and the stimulus manipulation, the authors interpret these events as related to separable processing stages for stimulus encoding, attention orientation, and decision (deliberation). This is largely consistent with previous findings from both event-related potentials (across trials) and single-trial estimates using decoding techniques and neural network approaches.  

Strengths:  

This work is not only important for the conceptual advance, but also in promoting this new analysis technique, which will likely prove useful in future research. For the broader picture, this work is an excellent example of the utility of neural measures for mental chronometry.  

We appreciate the very positive review and thank the reviewer for pointing out important weaknesses in our original manuscript and also providing resources to address them in the recommendations to authors. Below we comment on each identified weakness and how we addressed them.   

Weaknesses:  

(1) The manuscript would benefit from some conceptual clarifications, which are important for readers to understand this manuscript as a stand-alone work. This includes clearer definitions of Piéron's and Fechner's laws, and a fuller description of the EEG analysis technique.

We agree that the description of both laws were insufficient, we therefore added the following text in the last paragraph of the introduction:

“Piéron’s law predicts that the time to perceive the two stimuli (and thus the choice situation) should follow a negative power law with the stimulus intensity (Figure 1, green curve). In contradistinction, Fechner’s law states that the perceived difference between the two patches follows the logarithm of the absolute contrast of the two patches (Figure 1, yellow curve). As the task of our participants is to judge the contrast difference, Piéron’s law should predict the time at which the comparison starts (i.e. the stimuli become perceptible), while Fechner’s law should implement the comparison, and thus decision, difficulty”.

Regarding the EEG analysis technique we added a few elements at the start of the result:

“The hidden multivariate pattern model (HMP) implemented assumed that a task-related multivariate pattern event is represented by a half-sine whose timing varies from trial to trial based on a gamma distribution with a shape parameter of 2 and a scale, controlling the average latency of the event, free-to-vary per event (Weindel et al., 2024)”.

We also made the technique clearer at the start of the discussion:

“By modeling the recorded single-trial EEG signal between stimulus onset and response as a sequence of multivariate events with varying by-trial peak times, we aimed to detect recurrent events that contribute to the duration of the reaction time in the present perceptual decision-making task. In addition to the number of events, using this hidden multivariate pattern approach (Weindel et al., 2024) we estimated the trial-by-trial probability of each event’s peak, therefore accessing at which time sample each event was the most likely to occur”.

Additionally, we added a proper description in the method section (see the new first paragraph of the “Hidden multivariate pattern” subsection). 

(2) The manuscript, broadly, but the introduction especially, may be improved by clearly delineating the multiple aims of this project: examining the processes for decision-making, obtaining single-trial estimates of meaningful EEG-events, and whether central parietal positivity reflects ramping activity or steps averaged across trials.

For the sake of clarity we removed the question of the ramping activity vs steps in the introduction and focused on the processes in decision-making and their single-trial measurement as this is the main topic of the paper. Furthermore the references provided by the reviewer allowed us to write a more comprehensive review of previous studies and how the current study is in line with those. These changes are mainly manifested in these new sentences:

“As an example Philiastides et al. (2006) used a classifier on the EEG activity of several conditions to show that the strength of an early EEG component was proportional to the strength of the stimulus while a later component was related to decision difficulty and behavioral performance (see also Salvador et al., 2022; Philiastides and Sajda, 2006). Furthermore the authors interpreted that a third EEG component was indicative of the resource allocated to the upcoming decision given the perceived decision difficulty. In their study, they showed that it is possible to use single-trial information to separate cognitive processes within decision-making. Nevertheless, their method requires a decoding approach, which requires separate classifiers for each component of interest and restrains the detection of the components to those with decodable discriminating features (e.g. stimuli with strong neural generators such as face stimuli, see Philiastides et al., 2006)”.

(3) A fuller discussion of the limitations of the work, in particular, the absence of motor contributions to reaction time, would also be appreciated. 

As laid out in responses to comments R1.1 and R2 the new estimates now include evidence for a motor preparation component. We discuss this in the new “motor execution” paragraph in the discussion section. Additionally we discuss the limitation of the study and the method in the two last paragraphs of the discussion (in the new Section “Generalization and limitation”).

(4) At times, the novelty of the work is perhaps overstated. Rather, readers may appreciate a more comprehensive discussion of the distinctions between the current work and previous techniques to gauge single-trial estimates of decision-related activity, as well as previous findings concerning distinct processing stages in decision-making. Moreover, a discussion of how the events described in this study might generalise to different decision-making tasks in different contexts (for example, in auditory perception, or even value-based decision-making) would also be appreciated.  

We agree that the original text could be read as overstating. In addition to the changes linked to R3.2 we also now discuss the link with the previous studies in the before-last paragraph of the discussion before the conclusion in the new “Generalization and limitations” section:

“The present study showed what cognitive processes are contributing to the reaction time and estimated single-trial times of these processes for this specific perceptual decision-making task. The identified processes and topographies ought to be dependent on the task and even the stimuli (e.g. sensory events will change with the sensory modality). More complex designs might generate a higher number of cognitive processes (e.g. memory retrieval from a cue, Anderson et al., 2016) and so could more natural stimuli which might trigger other processes in the EEG (e.g. appraisal vs. choice as shown by Frömer et al., 2024). Nevertheless, the observation of early sensory vs. late decision EEG components is likely to generalize across many stimuli and tasks as it has been observed in other designs and methods (Philiastides et al., 2006; Salvador et al., 2022). To these studies we add that we can evaluate the trial-level contribution, as already done for specific processes (e.g. Si et al., 2020; Sturm et al., 2016), for the collection of events detected in the current study”.

Reviewing Editor Comments:  

As you will see, all three reviewers agree that the paper makes a valuable contribution and has many strengths. You will also see that they have provided a range of constructive comments highlighting potential issues with the interpretation of the outcomes of your signal decomposition method. In particular, all three reviewers point out that your results do not identify separate motor preparation signals, which we know must be operating on this type of task. The reviewers suggest further discussion of this issue and the potential limitations of your analysis approach, as well as suggesting some additional analyses that could be run to explore this further. While making these changes would undoubtedly enhance the paper and the final public reviews, I should note that my sense is that they are unlikely to change the reviewers' ratings of the significance of the findings and the strength of evidence in the final eLife assessment  

Reviewer #1 (Recommendations for the authors):  

(1) Abstract: "choice onset" is ill-defined and not the label most would give the start of the RT interval. Do you mean stimulus onset?  

We replaced with "choice onset" with "stimulus onset" in the abstract

(2) Similarly "choice elements" in the introduction seem to refer to sensory attributes/objects being decided about?  

We replaced "choice-elements" with "choice-relevant features of the stimuli"

(3) "how the RT emerges from these putative components" - it would be helpful to specify more what level of answer you're looking for, as one could simply answer "when they're done."  

We replaced with "how the variability in RTs emerges from these putative components"

(4) Line 61-62: I'm not sure this is a fully correct characterisation of Frömer et al. It was not similar in invoking a step function - it did not invoke any particular mechanism or function, and in that respect does not compare well to Latimer et al. Also, I believe it was the overlap of stimulus-locked components, not response-locked, that they argued could falsely generate accumulator-like buildup in the response-locked ERP.  

We indeed wrongly described Frömer et al. The sentence is now "In human EEG data, the classical observation of a slowly evolving centro-parietal positivity, scaling with evidence accumulation, was suggested to result from the overlap of time-varying stimulus-related activity in the response-locked event related potential"

(5) Line 78: Should this be single-trial *latency*?  

This referred to location in time but we agree that the term is confusing and thus replaced it with latencies.

(6) The caption of Figure 1 should state what is meant by the y-axis "time"  

We added the sentence "The y-axis refers the time predicted by each law given a contrast value (x-axis) and the chosen set of parameters." in the caption of Figure 1

(7) Line 107: Is this the correct description of Fechner's law? If the perceived difference follows the log of the physical difference, then a constant physical difference should mean a constant perceived difference. Perhaps a typo here.  

This was indeed a typo we replaced the corresponding part of the sentence with "the perceived difference between the two patches follows the logarithm of the absolute contrast of the two patches"

(8) Line 128: By scale, do you mean magnitude/amplitude?  

No, this refers to the parameter of a gamma distribution. To clarify we edited the sentence:  "based on a gamma distribution with a shape parameter of 2 and a scale parameter, controlling the average latency of the event, free-to-vary per event"

(9) The caption of Figure 3 is insufficient to make sense of the top panel. What does the inter-event interval mean, and why is it important to show? What is the "response" event?  

We agree that the top panel was insufficiently described. To keep the length of the paper short and because of the relatively low amount of information provided by these panels we replaced them for a figure only showing the average topographies as well as the asymmetry tests for each event.

(10) Figure 4: caption should say what the top vs bottom row represents (presumably, accuracy vs speed emphasis?), and what the individual dots represent, given the caption says these are "trial and participant averaged". A legend should be provided for the rightmost panels.  

We agree and therefore edited Figure 4. The beginning of the caption mentioned by the reviewer now reads: “A) The panels represent the average duration between events for each contrast level, averaged across participants and trials (stimulus and response respectively as first and last events) for accuracy (top) and speed instructions (bottom).”. Additionally we added legends for the SAT instructions and the model fits.

(11) Line 189: argued for a decision-making role of what?  

Stafford and Gurney (2004) proposed that Pieron’s law could reflect a non-linear transformation from sensory input to action outcomes, which they argued reflected a response mechanism. We (Van Maanen et al., 2012) specified this result by showing that a Bayesian Observer Model in which evidence for two alternative options was accumulated following Bayes Rule indeed predicted a power relation between the difference in sensory input of the two alternatives, and mean RT. However, the current data suggest that such an explanation cannot be the full story, as also noted by R3. To clarify this point we replaced the comment by the following sentence:

“Note that this observation is not necessarily incongruent with theoretical work that argued that Piéron’s law could also be a result of a response selection mechanism (Stafford and Gurney, 2004; Van Maanen et al., 2012; Palmer et al., 2005). It could be that differences in stimulus intensity between the two options also contribute to a Piéron-like relationship in the later intervals, that is convoluted with Fechner’s law (see Donkin and Van Maanen, 2014 for a similar argument). Unfortunately, our data do not allow us to discriminate between a pure logarithmic growth function and one that is mediated by a decreasing power function”.

(12) Table 2: There is an SAT effect even on the first interval, which is quite remarkable and could be discussed more - does this mean that the C1 component occurs earlier under speed pressure? This would be the first such finding.  

The original event we qualified as a P100 was sensitive to SAT but the earliest event is now the N40 and isn’t statistically sensitive to speed pressure in this data. We believe that the fact that the P100 is still sensitive to SAT is not a surprise and therefore do not outline it.

(13) Line 221: "decrease of activation when contrast (and thus difficulty) increases" - is this shown somewhere in the paper?  

The whole section for this analysis was rewritten (see comment below)

(14) I find the analysis of Figure 5 interesting, but the interpretation odd. What is found is that the peak of the decision signal aligns with the response, consistent with previous work, but the authors choose to interpret this as the decision signal "occurring as a short-lived burst." Where is the quantitative analysis of its duration across trials? It can at least be visually appraised in the surface plot, and this shows that the signal has a stimulus-locked onset and, apart from the slowest RTs, remains present and for the most part building, until response. What about this is burst-like? A peak is not a burst.  

This was the residue of a previous version of the paper where an analysis reported that no evidence accumulation trace was found. But after proper simulations this analysis turned out to be false because of a poor statistical test. Thus we removed this paragraph in the revised manuscript and Figure 5 has now been extended to include surface plots for all the events.

Reviewer #2 (Recommendations for the authors):  

Overall, I really enjoyed reading this paper. However, in some places the approach is a bit opaque or the results are difficult to follow. As I read the paper, I noted:  

Did you do a simple DDM, or did you do a collapsing bound for speed?  

The fitted DDM was an adaptation of the proportional rate diffusion model. We make this clearer at the end of the introduction: "Given that Fechner’s law is expected to capture decision difficulty we connected this law to the classical diffusion decision models by replacing the rate of accumulation with Fechner’s law in the proportional rate diffusion model of Palmer et al.(2005).”

It is confusing that the order of intervals in the text doesn't match the order in the table. It might be better to say what events the interval is between rather than assuming that the reader reconstructs.  

We agree and adapted the order in both the text and the table. The table is now also more explicit (e.g. RT instead of S-R)

Otherwise, I do wonder to what extent the method is able to differentiate processes that yield similar scalp topographies and find it a bit concerning that no motor component was identified.  

We believe that the new version with the LRP/CPP is a demonstration that the method can handle similar topographies. The method can handle events with close topographies as long as they are separate in time, however if they are not sequential to one another the method cannot capture both events. We now discuss this, in relation with the C1/P100 overlap, in the discussion section “Visual encoding time”:

“Nevertheless this event, seemingly overlapping with the P100 even at the trial level (Figure 5C), cannot be recovered by the method we applied. The fact that the P100 was recovered instead of the C1 could indicate that only the timing of the P100 contributes to the RT (see Section 3 of Weindel et al., 2024)”.

And we more generally address the question of overlap in the new section “Generalization and limitation”.

Reviewer #3 (Recommendations for the authors):  

Major Comments:  

(1) If we agree on one thing, it is that motor processes contribute to response time. Line 364: "In the case of decision-making, these discrete neural events are visual encoding, attention-orientation, and decision commitment, and their latency make up the reaction time." Does the third event, "decision commitment", capture both central parietal positivity (decision deliberation) and motor components? If so, how can the authors attribute the effects to decision deliberation as opposed to motor preparation?  

Thanks to the suggestions also in the public part. This main problem is now addressed as we do capture both a motor component and a decision commitment.

Line 351 suggests that the third event may contain two components.  

This was indeed our initial, badly written, hypothesis. Nevertheless the new solution again addresses this problem.

The time series in Figure 6 shows an additional peak that is not evident in the simulated ramp of Appendix 1.  

This was probably due to the overlap of both the CPP and the LRP. It is now much clearer that the CPP looks mostly like a ramp while the LRP looks much more like a burst-like/peaked activity. We make this clear in the “Decision event” paragraph of the discussion section:

“Regarding the build-up of this component, the CPP is seen as originating from single-trial ramping EEG activities but other work (Latimer et al., 2015; Zoltowski et al., 2019) have found support for a discrete event at the trial-level. The ERPs on the trial-by-trial centered event in Figure 5 show support for both accounts. As outlined above, the LRP is indeed a short burst-like activity but the build-up of the CPP between high vs low contrast diverges much earlier than its peak”.

Previous analyses (Weindel et al., 2024) found motor-related activity from central parietal topographies close to the response by comparing the difference in single-trial events on left- vs right-hand response trials. The authors suggest at line 315 that the use of only the right hand for responding prevented them from identifying a motor event.  

The use of only the right hand should have made the event more identifiable because the topography would be consistent across trials (rather than inverting on left vs right hand response trials).  

The reviewer is correct, in the original manuscript we didn’t test for lateralization, but the comment of the reviewer gave us the idea to explicitly test for the asymmetry (Figure 3). This test now clearly shows what would be expected for a motor event with a strong negativity over the left motor cortex.

The authors state on line 422 that the EEG data were truncated at the time of the response.  

Could this have prevented the authors from identifying a motor event that might overlap with the timing of the response?  

We thank the reviewer for this suggestion. This would have been a possibility but the problem is that adding samples after the response also adds the post-response processes (error monitoring, button release, stimulus disappearance, etc.). While increasing the samples after the response is definitely something that we need to inspect, we think that the separation we achieved in this revision doesn’t call for this supplementary analysis.

The largest effects of contrast on the third event amplitude appear around the peak as opposed to the ramp. If the peak is caused by the motor component, how does this affect the conclusions that this third event shows a decision-deliberation parietal processes as opposed to a motor process (a number of studies suggest a causal role for motor processes in decision-making e.g. Purcell et al., 2010 Psych Rev; Jun et al., 2021 Nat Neuro; Donner et al., 2009 Curr Bio).  

This result now changed and it does look like the peak capturing most of the effect is no longer true. We do however think that there might be some link to theories of motor-related accumulation. We therefore added this to the discussion in the Motor execution section:

“Based on all these observations, it is therefore very likely that this LRP event signs the first passage of a two-step decision process as suggested by recent decision-making models (Servant et al., 2021; Verdonck et al., 2021; Balsdon et al., 2023)”.

I would suggest further investigation into the motor component (perhaps by extending the time window of analysed EEG to a few hundred ms after the response) and at least some discussion of the potential contribution of motor processes, in relation to the previous literature.  

We believe that the absence of a motor component is sufficiently addressed in the revised manuscript and in the responses to the other comments.    

(2) What do we learn from this work? Readers would appreciate more attention to previous findings and a clearer outline of how this work differs. Two points stand out, outlined below. I believe the authors can address these potential complaints in the introduction and discussion, and perhaps provide some clarification in the presentation of the results.  

In the introduction, the authors state that "... to date, no study has been able to provide single-trial evidence of multiple EEG components involved in decision-making..." (line 64). Many readers would disagree with this. For example, Philiastides, Ratcliff, & Sadja (2006) use a single-trial analysis to unravel early and late EEG components relating to decision difficulty and accuracy (across different perceptual decisions), which could be related to the components in the current work. Other, network-based single-trial EEG analyses (e.g., Si et al., 2020, NeuroImage, Sturn et al., 2016 J Neurosci Methods) could also be related to the current component approach. Yet other approaches have used inverse encoding models to examine EEG components related to separable decision processes within trials (e.g., Salvador et al., 2022, Nat Comms). The results of the current work are consistent with this previous work - the two components from Philiastides et al., 2006 can be mapped onto the components in the current work, and Salvador et al., 2022 also uncover stimulus- and decision-deliberation related components.  

We completely agree with the reviewer that the link to previous work was insufficient. We now include all references that the reviewer points out both in the introduction (see response R3.2) and in the discussion (see response R3.4). We wish to thank the reviewer for bringing these papers to our attention as they are important for the manuscript.

The authors relate their components to ERPs. This prompts the question of whether we would get the same results with ERP analyses (and, on the whole, the results of the current work are consistent with conclusions based on ERP analyses, with the exception of the missing motor component). It's nice that this analysis is single-trial, but many of the follow-up analyses are based on grouping by condition anyway. Even the single-trial analysis presented in Figure 4 could be obtained by median splits (given the hypotheses propose opposite directions of effects, except for the linear model). 

We do not agree with the reviewer in the sense that classical ERP analyses would require much more data-points. The performance of the method is here to use the information shared across all contrast levels to be able to model the processing time of a single contrast level (6 trials per participant). Furthermore, as stated in the response to R1.4 and R1.5, the aim of the paper is to have the time of information processing components which cannot be achieved with classical ERPs without strong, and likely false, assumptions.

Medium Comments:  

(1) The presentation of Piéron's law for the behavioural analysis is confusing. First, both laws should be clearly defined for readers who may be unfamiliar with this work. I found the proposal that Piéron's law predicts decreasing RT for increasing pedestal contrast in a contrast discrimination paradigm task surprising, especially given the last author's previous work. For example, Donkin and van Maanen (2014) write "However, the commonality ofPiéron's Law across so many paradigms has lead researchers (e.g., Stafford & Gurney, 2004; Van Maanen et al., 2012) to propose that Piéron's Law is unrelated to stimulus scaling, but is a result of the architecture of the response selection (or decision making) process." The pedestal contrast is unrelated to the difficulty of the contrast discrimination task (except for the consideration of Fechner's law). Instead, Piéron's law would apply to the subjective difference in contrast in this task, as opposed to the pedestal contrast. The EEG results are consistent with these intuitions about Piéron's law (or more generally, that contrast is accumulated over time, so a later EEG component for lower pedestal contrast makes sense): pedestal contrast should lead to faster detection, but not necessarily faster discrimination. Perhaps, given the complexity of the manuscript as a whole, the predictions for the behavioural results could be simplified?  

We agree that the initial version was confusing. We now clarified the presentation of Piéron's law at the end of the introduction (see also response to R2).

Once Fechner's law is applied, decision difficulty increases with increasing contrast, so Piéron's law on the decision-relevant intensity (perceived difference in contrast) would also predict increasing RT with increasing pedestal contrast. It is unlikely that the data are of sufficient resolution to distinguish a log function from a power of a log function, but perhaps the claim on line 189 could be weakened (the EEG results demonstrate Piéron's law for detection, but do not provide evidence against Piéron's law in discrimination decisions).  

This is an excellent observation, thank you for bringing it to our attention. Indeed, the data support the notion that Pieron’s law is related to detection, but do not rule out that it is also related to decision or discrimination. In earlier work, we (Donkin & Van Maanen, 2014) addressed this question as well, and reached a similar conclusion. After fitting evidence accumulation models to data, we found no linear relationship between drift rates and stimulus difficulty, as would have been the case if Pieron's law could be fully explained by the decision process (as -indirectly- argued by Stafford & Gurney, 2004; Van Maanen et al., 2012). The fact that we observed evidence for a non-linear relationship between drift rates and stimulus difficulty led us to the same conclusion, that Pieron’s law could be reflected in both discrimination and decision processes. We added the following comment to the discussion about the functional locus of Pieron's law to clarify this point:

“Note that this observation is not necessarily incongruent with theoretical work that argued that Piéron’s law could also be a result of a response selection mechanism (Stafford and Gurney, 2004; Van Maanen et al., 2012; Palmer et al., 2005). It could be that differences in stimulus intensity between the two options also contribute to a Piéron like relationship in the later intervals, that is convoluted with Fechner’s law (see Donkin and Van Maanen, 2014, for a similar argument). Unfortunately, our data do not allow us to discriminate between a pure logarithmic growth function and one that is mediated by a decreasing power function”.

(2) Appendix 1 shows that the event detection of the HMP method will also pick up on ramping activity. The description of the problem in the introduction is that event-like activity could look like ramping when averaged across trials. To address this problem, the authors should simulate events (with some reasonable dispersion in timing such that they look like ramping when averaged) and show that the HMP method would not pull out something that looked like ramping. In other words, the evidence for ramping in this work is not affected by the previously identified confounds.  

We agree that this demonstration was necessary and thus added the suggested simulation to Appendix 1. As can be seen in the Figure 1 of the appendix, when we simulate a half-sine the average ERP based on the timing of the event looks like a half-sine.

(3) Some readers may be interested in a fuller discussion of the failure of the Fechner diffusion model in the speed condition.  

We are unsure which failure the reviewer refers to but assumed it was in relation to the behavioral results and thus added: 

It is unlikely that neither Piéron nor Fechner law impact the RT in the speed condition. Instead this result is likely due to the composite nature of the RT where both laws co-exist in the RT but cancel each other out due to their opposite prediction.

Minor Comments:  

(1) "By-trial" is used throughout. Normally, it is "trial-by-trial" or "single-trial" or "trial-wise".

We replaced all occurrences of “by-trial”  with the three terms suggested were appropriate.

(2) Line 22: "The sum of the times required for the completion of each of these precessing steps is the reaction time (RT)." The total time required. Processing.  

Corrected for both.

(3) Line 26/27: "Despite being an almost two century old problem (von Helmholtz, 2021)." Perhaps the citation with the original year would make this point clearer.  

We agree and replaced the citation.

(4) Line 73: "accounted by estimating". Accounted for by estimating.  

Corrected.

(5) Line 77 "provides an estimation on the." Of the.  

Corrected.

(6) Line 86: "The task of the participants was to answer which of two sinusoidal gratings." The picture looks like Gabor's? Is there a 2d Gaussian filter on top of the grating? Clarify in the methods, too.  

We incorrectly described the stimuli as those were indeed just Gabor’s. This is now corrected both in the main text and the method section.

(7) Figure 1 legend: "The Fechner diffusion law" Fechner's law or your Fechner diffusion model?  

Law was incorrect so we changed to model as suggested.

(8) Line 115: "further allows to connects the..." Allows connecting the.  

Corrected.

(9) Line 123: "lower than 100 ms or higher than..." Faster/slower.  

Corrected.

(10) Line 131: "To test what law." Which law.?  

Corrected to model.

(11) Figure 2 legend: "Left: Mean RT (dot) and average fit (line) over trials and participants for each contrast level used." The fit is over trials and participants? Each dot is? Average trials for each contrast level in each participant?  

This sentence was corrected to “Mean RT (dot) for each contrast level and averaged predictions of the individual fits (line) with Accuracy (Top) and Speed (Bottom) instructions.”.

(12) Line 231: "A comprehensive analysis of contrast effect on". The effect of contrast on.  

This title was changed to “functional interpretation of the events”.

(13) Line 23: "the three HMP event with". Three HMP events.

The sentence no longer exists in the revised manuscript.

(14) Line 270: "Secondly, we computed the Pearson correlation coefficient between the contrast averaged proportion of correct." Pearson is for continuous variables. Proportion correct is not continuous. Use Spearman, Kendall, or compute d'.  

The reviewer rightly pointed out our error, we corrected this by computing Spearman correlation.

(15)  Line 377: "trial 𝑛 + 1 was randomly sampled from a uniform distribution between 0.5 and 1.25 seconds." It's just confusing why post-response activity in Figure 5 does look so consistent. Throughout methods: "model was fitted" should be "was fit", and line 448, "were split".  

We do not have a specific hypothesis of why the post-response activity in the previous Figure 5 was so consistent. Maybe the Gaussian window (same as in other manuscripts with a similar figure, e.g. O’Connell et al. 2012) generated this consistency. We also corrected the errors mentioned in the methods.

(16) The linear mixed models paragraph is a bit confusing. Can it clearly state which data/ table is being referred to and then explain the model? "The general linear mixed model on proportion of correct responses was performed using a logit link. The linear mixed models were performed on the raw milliseconds scale for the interval durations and on the standardized values for the electrode match." We go directly from proportion correct to raw milliseconds...  

The confusion was indeed due to the initial inclusion of a general linear mixed model on proportion correct which was removed as it was not very informative. The new revision should be clearer on the linear mixed models (see first sentence of subsection ‘linear mixed models' in the method section).

(17) A fuller description of the HMP model would be appreciated.  

We agree that this was necessary and added the description of the HMP model in the corresponding method section “Hidden multivariate pattern” in addition to a more comprehensive presentation of HMP in the first paragraph of the Result and Discussion sections.

(18) Line 458: "Fechner's law (Fechner, 1860) states that the perceived difference (𝑝) between the two patches follows the logarithm of the difference in physical intensity between..." ratio of physical intensity.  

Corrected.

(19) P is defined in equations 2 and 4. I would include the beta in equation 4, like in equation 2, then remove the beta from equations 3 and 5 (makes it more readable). I would also just include the delta in equation 2, state that in this case, c1 = c+delta/2 or whatever.  

This indeed makes the equation more readable so we applied the suggestions for equations 2, 3, 4 and 5. The delta was not added in equation 2 but instead in the text that follows:

“Where 𝐶1 = 𝐶0 + 𝛿, again with a modality and individual specific adjustment slope (𝛽).” 

(20) The appendix suggests comparing the amplitudes with those in Figure 3, but the colour bar legend is missing, so the reader can only assume the same scale is used?  

We added the color bar as it was indeed missing. Note though that the previous version displayed the estimation for the simulated data while this plot in the revised manuscript shows the solution on real data obtained after downsampling the data (and therefore look for a larger pattern as in the main text). We believe that this representation is more useful given that the solution for the downsampled data is no longer the same as the one in the main text (due to the difference in pattern width).

This passage explains that when we watch certain media styles over and over, we start using them to understand real life. If a news show always shows loud, heated arguments, viewers may think that’s the “normal” way to handle disagreements. Media formats can quietly shape how people act and communicate.

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

We are grateful to the reviewers for their thoughtful and constructive evaluations of our manuscript. Their comments helped us clarify key aspects of the study and strengthen both the presentation and interpretation of our findings. The central goal of this work is to dissect how the opposing activities of GATA4 and CTCF coordinate chromatin topology and transcriptional timing during human cardiomyogenesis. The reviewers’ feedback has allowed us to refine this message and better contextualize our results within the broader framework of chromatin regulation and cardiac development.

In response to the reviews, in our preliminary revision we have already implemented substantial improvements to the manuscript, including additional analyses, clearer data visualization, and revisions to the text to avoid overinterpretation. These refinements enhance the robustness of our conclusions without altering the overall scope of the study. A small number of additional analyses and experiments are ongoing and will be added to the full revision, as detailed below.

We believe that the revised manuscript, together with the planned updates, fully addresses the reviewers’ concerns and substantially strengthens the contribution of this work to the field.

Reviewer 1 – Point 1:

In the datasets you are examining, what are the relative percentages in each of the four groups relating compartmentalization change to expression change (A→B, expression up; A→B, down; B→A, up; B→A, down)?

We quantified compartment–expression relationships using Hi-C and bulk RNA-seq from H9 ESCs and CMs. The percentages for each category are shown below and incorporated into updated Figure S2H.

Group

Downregulated in CM

Upregulated in CM

A-to-A

11.92%

8.44%

A-to-B

18.20%

2.79%

B-to-A

7.96%

18.07%

B-to-B

14.36%

6.44%

A chi-squared test comparing observed vs. expected distributions (based on gene density across bins) confirmed a strong association between compartment dynamics and transcriptional behavior. B-to-A genes are significantly enriched among genes upregulated in CMs, while A-to-B genes are enriched among those downregulated (updated Figure S2H).

We next assessed with GSEA how these gene classes respond to GATA4 and CTCF knockdown. In 2D CMs, GATA4 knockdown reduces expression of CM-upregulated B-to-A genes and increases expression of CM-downregulated A-to-B genes, whereas CTCF knockdown produces the opposite pattern (updated Figure 2F).

Applying the same analysis to cardioid bulk RNA-seq (updated Figure 4E) revealed the strongest effects in SHF-RV organoids, consistent with monolayer data. In SHF-A organoids, only GATA4 knockdown had a measurable impact on CM-upregulated B-to-A and CM-downregulated A-to-B genes. Because the subsets of CM-downregulated B-to-A and CM-upregulated A-to-B genes were very small and showed no consistent trends, Figure 4 focuses on the two informative categories only. The full classification is provided in Reviewer Figure 1 below.

(The figure cannot be rendered in this text-only format)

Reviewer Figure 1. GSEA for CM-upregulated B-to-A and CM-downregulated A-to-B genes. p-values by Adaptive Monte-Carlo Permutation test.

Reviewer 1 – Point 2

This phrase in the abstract is imprecise: ‘whereas premature CTCF depletion accelerates yet confounds cardiomyocyte maturation.’

---

The abstract has been revised to: “whereas premature CTCF depletion accelerates yet alters cardiomyocyte maturation.” (lines 29-30).

Reviewer 1 – Point 3

Regarding this statement: "Disruption of [3D chromatin architecture] has been linked to genetic dilated cardiomyopathy (DCM) caused by lamin A/C mutations8,9, and mutations in chromatin regulators are strongly enriched in de novo congenital heart defects (CHD)10, underscoring their pathogenic relevance11." The first studies to implicate chromatin structural changes in heart disease, including the role of CTCF in that process, were PMID: 28802249, a model of acquired, rather than genetic, disease.

We added the following sentence to the paragraph introducing CTCF: “Moreover, depletion of CTCF in the adult cardiomyocytes leads to heart failure28,29.” (line 72)

Reviewer 1 – Point 4

Can you quantify this statement: ‘the compartment switch coincided with progressive reduction of promoter–gene body interactions’?

We quantified promoter–gene body contacts by calculating the area under the curve (AUC) of the virtual 4C signal derived from H9 Hi-C data across differentiation. As a result of this analysis we added the following sentence: “Quantitatively, interactions between the TTN promoter and its gene body decreased by ~55% from the pluripotent stage to day 80 cardiomyocytes.” (lines 89-91).

Reviewer 1 – Point 5

Regarding this statement: "six regions became less accessible in CMs, correlating with ChIP-seq signal for the ubiquitous architectural protein CTCF." I don't see 6 ATAC peaks in either TTN trace in Figure 1A.

We corrected the text as it follows: “TTN experienced clear changes in chromatin accessibility during CM differentiation: ATAC-seq identified two CM-specific peaks that correlated with ChIP-seq signal for the cardiac pioneer TF GATA4 at the two promoters, one driving full length titin and the other the shorter cronos isoform. In contrast, two regions became less accessible in CMs, correlating with two of the six ChIP-seq peaks for the ubiquitous architectural protein CTCF” (lines 93-97). We attribute the differences between ChIP-seq and ATAC-seq profiles to methodological sensitivity and/or biological variability between datasets generated in different laboratories and cell batches.

Reviewer 1 – Point 6

Western blots need molecular weight markers.

We edited the relevant panels accordingly (updated Figures 1E and 2B).

Reviewer 1 – Point 7

Regarding this statement: "The decrease in CTCF protein levels may explain its selective detachment from TTN during cardiomyogenesis." At face value, these findings suggest the opposite: i.e. that a massive downregulation of CTCF at protein level should affect its binding across the genome, which is not tested and is hard to evaluate between ChIP-seq studies from different groups and from different developmental timeframes.

We revised the text to avoid implying selective detachment and performed a genome-wide analysis of CTCF occupancy using ENCODE ChIP-seq datasets generated by the same laboratory with matched protocols in hESCs and hESC-derived CMs. This analysis shows that 43.2% of CTCF sites present in ESCs are lost in CMs, whereas only 5.7% are gained, confirming a broad reduction in CTCF binding during differentiation. These results are now included in__ updated Figure 1B__.

Reviewer 1 – Point 8a

A couple thoughts on the FISH experiments in Figure 2. A claim of 'impaired B-A transition' would be more convincing if you show, by FISH, that the relative distance of TTN from lamin B increases with differentiation.

Although prior work from us and others has established that TTN transitions from the nuclear periphery in hESCs to a more internal position during cardiomyogenesis (Poleshko et al. 2017; Bertero et al. 2019a), we are reproducing this trajectory in WTC11 hiPSCs as part of the FISH experiments for the full revision.

__Reviewer 1 – Point 8b __

In the [FISH] images: are you showing a total projection of all z planes? One assumes the quantitation is relative to a 3D reconstruction in which the lamin B signal is restricted to the periphery. Have you shown this? __

Quantification was performed on full 3D reconstructions from Z-stacks, as detailed in the Methods (lines 721-727). While the original submission displayed maximum-intensity projections, updated Figure 2D and Figure S2E now show representative single optical sections, which more clearly highlight the spatial relationship between the TTN locus and the nuclear lamina.

Reviewer 1 – Point 8c

Lastly, these data are very interesting and important, provoking reexamination of your interpretation of the results in Figure 1. Figure 1 was interpreted to show that less CTCF binding led to decreased lamina (and thus B compartment) association during development. Figure 2 shows that depleting CTCF does not change association of TTN with lamina.

Our interpretation is that by day 25 of hiPSC-CM differentiation the TTN locus may have reached its maximal radial repositioning even in control cells, limiting the ability to detect earlier effects of CTCF depletion. To test whether CTCF knockdown accelerates lamina detachment at earlier stages, we are repeating the FISH analysis for the inducible CTCF knockdown line at multiple time points during differentiation.

Reviewer 1 – Point 9

A thought about this statement: "Altogether, these results suggest that GATA4 and CTCF function as positive and negative regulators of B-to-A compartment switching, likely acting through global and local chromatin remodeling, respectively." GATA4 induces TTN expression and its knockdown prevents TTN expression-the evidence that GATA4 affects compartmentalization is unclear. By activating the gene, GATA4 may shift TTN to B classification.

Our current data do not allow us to disentangle whether GATA4-driven transcriptional activation precedes or follows the B-to-A compartment shift. We have therefore removed the mechanistic speculation from this sentence to avoid overinterpretation. Nevertheless, the analyses in updated Figure 2F, discussed in the response to Reviewer 1 - Point 1, show that GATA4 knockdown preferentially reduces expression of CM-upregulated B-to-A genes, while CTCF knockdown has the opposite effect, supporting the conclusion that both factors influence the transcriptional programs associated with B-to-A transitions.

Reviewer 1 – Point 10

__I'm not sure what I am looking at in Figure 3C. Are those traces integration of interactions over a defined window? "Each [mutant is] clearly different from WT" is not obvious from the presentation. The histograms are plotting AUC of what? Interactions of those peaks with the mutated region? I genuinely appreciate how laborious this experiment must have been and encourage you to explain better what you are showing. __

We revised the main text to avoid overstating the differences (“clearly” “in a similar manner”, line 192) and expanded the l__egends of updated Figures 3C–D__ to clarify what is being shown: “(C) 4C-seq in hiPSCs using the promoter-proximal region of TTN as viewpoint. The top panel shows raw interaction profiles. The lower panels plot pairwise differences between conditions to reveal subtle changes. A schematic indicating the 4C viewpoint is included for clarity. Right inset: zoom of the CBS4–5 region. Mean of n = 3 cultures. (D) AUC of the differential 4C-seq signal for defined intervals (panel C). p-values by one-sample t-test against μ = 0.”. We also added a visual cue in updated Figure 3C indicating the 4C viewpoint to facilitate interpretation.

Reviewer 1 – Point 11

Again acknowledging how challenging these experiments are: when you mutant a locus, you change CTCF binding but you also change the DNA. Thus, attributing the changes in interactions to presence/absence of CTCF binding is difficult, because the DNA substrate itself has changed. Perhaps you are presenting all of this as a negative result, given the modest effect on transcription, which is as important as a positive result, given the assumptions usually made about such things. But the results are not clearly described and your interpretation seems to go between implying the structural change causative and being agnostic.

We recognize that deleting a genomic region can affect both CTCF binding and the DNA substrate itself. For this reason, we implemented two parallel genome-editing strategies:

(1) a straightforward Cas9-mediated deletion of ~100 bp centered on each CBS, and

(2) a more precise HDR approach replacing only the 20 bp core CTCF motif.

Because the HDR strategy succeeded, all downstream analyses were carried out on these minimal edits, which substantially limit disruption of other transcription factor motifs and reduce the likelihood of sequence-dependent polymer effects unrelated to CTCF.

Nevertheless, to avoid implying unwarranted causality in the absence of more conclusive evidence, we added a paragraph to the Discussion outlining these limitations, including the sentence: “Our study also reflects general challenges in separating chromatin-architectural and transcriptional mechanisms. Although the CBS edits were restricted to the core CTCF motifs, additional sequence-dependent effects cannot be fully excluded, and we therefore interpret the resulting changes as consistent with—but not exclusively due to—loss of CTCF binding.” (lines 365-368)

Reviewer 1 - Point 12.

Figure 4C: since you have RNA-seq data, a much more objective way to present these data would be to show all data (again, A-B, up; A-B, down; B-A, up; B-A, down) and the effects of CTCF or GATA4. Regardless, you can still focus on the cardiac specific genes. But my guess is if you examine all genes, the pattern you show in panel C will not be present in the majority of cases. Furthermore, if this hypothesis is wrong, such an analysis will allow you to identify other genes affected by the mechanisms you describe and your analysis will test whether these mechanisms are in fact conserved at different loci.

As outlined in our response to Point 1, we extended the analysis to all genes undergoing compartment changes and incorporated this into the cardioid RNA-seq dataset. This revealed a clear and consistent relationship between GATA4 or CTCF knockdown and the expression of B-to-A and A-to-B gene classes (updated Figure 4E).

Reviewer 2 - Point 1.1

1. CTCF regulation at TTN locus:

(1) Figure 1A: The claim of the authors about convergent CTCF sites and transcriptional activation of TTN is quite simplistic. This claim is only valid when we know where cohesin is loaded. If cohesin is loaded at then intragenic GATA4 binding site, then the only important CTCF sites is at the promoter of TTN. I suggest that the authors read few more publications which may help the authors to better understand how cohesin and CTCF team up to regulate transcription, such as Hsieh et al., Nature Genetics, 2022; Liu et al., Nature Genetics, 2021; Rinzema et al., Nature Structural and Molecular Biology, 2022.

__Suggestion: The authors should add cohesin (RAD21/SMC1A) and NIPBL ChIP-seq for better interpretation. __

In line with the reviewer’s insightful suggestion, we integrated cohesin ChIP-seq data into updated Figure 1A. Specifically, we added a RAD21 ChIP-seq track from hESCs, which provides direct evidence of cohesin occupancy across the TTN locus. RAD21 binding closely parallels CTCF binding at five sites within the gene body, supporting a model in which promoter-proximal CTCF anchors cohesin to stabilize repressive loops at this locus. This analysis substantially strengthens the mechanistic framework and is consistent with the studies recommended by the reviewer, which we have now cited (lines 68 and 104).

Reviewer 2 - Point 1.2. (2) Figure 3B: If delta2CBS only has heterozygenous deletion of CBS6, why we would expect the binding will be weaken to 50%. However, the CTCF binding is reduced to around 1/10 in the ChIP-qPCR. How do the authors explain this?

Sequencing of the Δ2CBS line shows that one CBS6 allele carries the intended EcoRI replacement, while the second allele contains a 2-bp deletion within the core CTCF motif (Figure S3C). Remarkably, this small deletion is sufficient to abolish CTCF binding, resulting in complete loss of occupancy at CBS6 despite heterozygosity. We clarified this in the text as follows: “CTCF ChIP-qPCR in hiPSCs confirmed complete loss of CTCF binding at the targeted sites, including CBS6 in the Δ2CBS line, indicating that the 2-bp deletion sufficed to disrupt CTCF binding while occupancy at other CBSs remained unaffected.” (lines 187–189).

Reviewer 2 - Point 1.3a (3) Figure 3C: There are two problems with the 4C experiments: (a) The changes are really mild. In fact, none of the p-values in Figure 3D are significant.

The effect of deleting CBS1 is indeed modest, consistent with reports that individual CTCF binding sites often show functional redundancy (i.e., Rodríguez-Carballo et al. 2017; Barutcu et al. 2018; Kang et al. 2021). Nevertheless, our 4C-seq experiments have reproducibly shown the same directional trend across biological replicates. To increase statistical power and more rigorously assess the robustness of this effect, we are generating additional 4C replicates as part of the full revision.

Reviewer 2 - Point 1.3b [In the 4C experiments] (b) The authors should also consider a model that CTCF directly serves as a repressor. In this way, 3D genome may not be involved. B-A switch is simply caused by the activation of the locus.

We now explicitly acknowledge this possibility in the Discussion. The revised text states: “Moreover, our data cannot unambiguously separate CTCF’s architectural role from potential direct repressive activity. Both mechanisms could contribute to the observed effects, and our findings likely reflect the combined influence of CTCF on chromatin topology and gene regulation.” (lines 368–371).

Reviewer 2 - Point 2.1a 2. __(CTCF) detachment: The authors mentioned few times "detachment". In the context of this manuscript, the authors indicate detachment from nuclear lamina. However, the authors haven't provide convincing evidence about this. __

In the two instances where we used the term “detachment,” we intended it to refer exclusively to reduced CTCF binding to DNA, not to lamina repositioning. To avoid ambiguity, we have replaced “detachment” with “reduced binding” in both locations (lines 123 and 329). We do not use this term to describe TTN–lamina positioning.

Reviewer 2 - Point 2.1b (1) Figure 1D: I doubt whether such changes of CTCF protein abundance will lead to LAD detachment. Suggest the authors read van Schaik et al., Genome Biology, 2022. With the full depletion of CTCF, the effects on LADs are still very restricted.

We agree that the observed correlation between reduced CTCF levels and the relocation of TTN away from a LAD does not establish causality. As outlined in our response to Reviewer 1 – Point 8c, we are performing additional FISH experiments at earlier differentiation stages in the CTCF inducible knockdown line to directly assess whether partial CTCF depletion is sufficient to alter the timing of TTN–lamina separation.

Reviewer 2 - Point 2.2 (2) Figure 2D: Lamin B1 should be mostly at nuclear periphery. I have few questions: (1) is the antibody specific? (2) do these cells carry mutation in LMNB1 gene? (3) is the staining actually LMNA?

As also clarified in response to Reviewer 1 – Point 8b, the original images displayed maximum-intensity projections of Z-stacks, which obscured the peripheral distribution of LMNB1. We have updated Figure 2D and Figure S2E to show representative individual optical sections, which more clearly display the expected peripheral LMNB1 signal. We also confirm that the antibody used is specific for LMNB1 and previously validated (Bertero et al. 2019b), and that the WTC11-derived lines used in this study carry no mutation in LMNB1.

Reviewer 2 - Point 3

3. Opposite functions of GATA4 and CTCF: These data in Figure 5E-H argues the opposite role of GATA4 and CTCF in transcriptional regulation. Would it be that CTCF KD just affected cell proliferation, which is actually known for many cell types, rather than affect CM differentiation process? If this is the reason, inversed correlation between CTCF KD and GATA4 KD in Figure 4D could also be explained by opposite effects on cell cycle.

We directly evaluated this possibility. In FHF–LV cardioids, cell cycle profiling in Figure 6C and Figure S6C (now S7C) showed that CTCF knockdown does not alter the distribution of CMs across G1/S/G2–M phases, in contrast to the marked increase in proliferation observed with GATA4 knockdown.

Because this comment referred specifically to the SHF data, we also analyzed mitotic gene expression in the SHF–RV bulk RNA-seq dataset using GSEA. CTCF knockdown did not significantly enrich any cell cycle–related gene sets, whereas GATA4 knockdown produced a strong enrichment for mitotic cell cycle terms, in line with FHF-LV data (Reviewer Figure 2).

These results are summarized in updated Figure S5C, reporting also the results of the broader GSEA analysis, and together indicate that the transcriptional divergence between CTCF and GATA4 knockdown is not simply explained by opposing effects on proliferation.

(The figure cannot be rendered in this text-only format)

Reviewer Figure 2. GSEA for mitotic cell cycle in SHF-RV after inducible knockdown of CTCF (left) or GATA4 (right). p-values by Adaptive Monte-Carlo Permutation test.

Reviewer 2 - Point 4 4. In discussion, the authors suggested that CTCF is a local chromatin remodeller. In my view, association with local chromatin compaction doesn't qualify CTCF as a chromatin remodeler. To my knowledge, CTCF does not have an enzymatic domain, then how does it remodel chromatin?

Our intended meaning was that CTCF shapes 3D chromatin architecture through its role in organizing intergenic looping, not that it remodels chromatin enzymatically. To avoid confusion, we have removed the original sentence from the Discussion.

Reviewer 2 - Point 5. 5. Some conclusions are drawn based on insignificant p-values, e.g. Figure 2F, Figure 3D, etc. The authors should be careful about their conclusion, and tone down their statement for the observations have borderline significance.

The conclusions based on bulk RNA-seq have been revised in response to Reviewer 1 – Point 1 (updated Figure 2F). By subsetting B-to-A and A-to-B genes according to their expression dynamics, this analysis now yields clearer and statistically significant differences between conditions.

Regarding the 4C-seq data, as acknowledged in Reviewer 2 – Point 3a, the observed effects are modest. We are generating additional biological replicates to increase statistical power. In the meantime, we have adjusted the text to avoid overstating these findings. The revised manuscript now states: “While the difference did not reach significance, these trends suggest …” (lines 199–200).

Reviewer 2 - Minor comment 1. Minor comments: 1. Figure 1A: (1) I suggest to label two promoters in the gene model. It's unclear in the figure in the current version; (2) I was a bit confused with the way how the authors labeled CTCF directionality. I thought there are a lot of promoters. Why didn't they use triangles?

We updated Figure 1A to label both TTN promoters and indicate their orientation. For CTCF sites, we now clearly display the motif direction and core binding region as determined by FIMO analysis of the CTCF ChIP-seq peaks, improving consistency and interpretability.

Reviewer 2 - Minor comment 2. 2. Figure 2C: I think the drastical reduction of titin-mEGFP levels is only due to the way how the authors analyze their FACS data. Can the author quantify on median fluorescence intensity?

The gating strategy for titin-mEGFP⁺ cells was defined using a reporter-negative control, and cells lacking TNNT2 expression showed no detectable titin-mEGFP signal, confirming the specificity of the gate. To complement this analysis, we also quantified the median fluorescence intensity (MFI) of titin-mEGFP⁺ cells. The MFI analysis corroborates the original findings, showing a significant decrease in GATA4 knockdown and an increase in CTCF knockdown (updated Figure S2D).

__Reviewer 2 - Minor comment 3. 3. Figure S2G: P value should be -log10, I assume. Please label it accurately. __

We appreciate the reviewer pointing out this labeling error. In the revised manuscript, this panel has been removed to accommodate the updated compartment–expression analysis now presented in updated Figure 2H (see response to Reviewer 1 – Point 1), and the issue is no longer applicable.

References

Barutcu AR, Maass PG, Lewandowski JP, Weiner CL, Rinn JL. 2018. A TAD boundary is preserved upon deletion of the CTCF-rich Firre locus. Nat Commun 9: 1444.

Bertero A, Fields PA, Ramani V, Bonora G, Yardımcı GG, Reinecke H, Pabon L, Noble WS, Shendure J, Murry CE. 2019a. Dynamics of genome reorganization during human cardiogenesis reveal an RBM20-dependent splicing factory. Nature communications 10: 1538.

Bertero A, Fields PA, Smith AS, Leonard A, Beussman K, Sniadecki NJ, Kim D-H, Tse H-F, Pabon L, Shendure J, et al. 2019b. Chromatin compartment dynamics in a haploinsufficient model of cardiac laminopathy. Journal of Cell Biology 218: 2919–44.

Kang J, Kim YW, Park S, Kang Y, Kim A. 2021. Multiple CTCF sites cooperate with each other to maintain a TAD for enhancer–promoter interaction in the β-globin locus. The FASEB Journal 35: e21768.

Poleshko A, Shah PP, Gupta M, Babu A, Morley MP, Manderfield LJ, Ifkovits JL, Calderon D, Aghajanian H, Sierra-Pagán JE, et al. 2017. Genome-Nuclear Lamina Interactions Regulate Cardiac Stem Cell Lineage Restriction. Cell 171: 573–587.

Rodríguez-Carballo E, Lopez-Delisle L, Zhan Y, Fabre PJ, Beccari L, El-Idrissi I, Huynh THN, Ozadam H, Dekker J, Duboule D. 2017. The HoxD cluster is a dynamic and resilient TAD boundary controlling the segregation of antagonistic regulatory landscapes. Genes Dev 31: 2264–2281.

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Referee #2

Evidence, reproducibility and clarity

Becca et al. characterized the functions of GATA4 and CTCF in the context of cardiomyogenesis. The authors aim to establish a link between 3D genome changes (A/B compartment and long-range chromatin interactions) and activation of cardiac specific genes such as TTN. They showed opposite effects of GATA4 and CTCF in regulating these genes as well as phenotypical traits. I have the following suggestions and questions:

Major comments:

1. CTCF regulation at TTN locus:

(1) Figure 1A: The claim of the authors about convergent CTCF sites and transcriptional activation of TTN is quite simplistic. This claim is only valid when we know where cohesin is loaded. If cohesin is loaded at then intragenic GATA4 binding site, then the only important CTCF sites is at the promoter of TTN. I suggest that the authors read few more publications which may help the authors to better understand how cohesin and CTCF team up to regulate transcription, such as Hsieh et al., Nature Genetics, 2022; Liu et al., Nature Genetics, 2021; Rinzema et al., Nature Structural and Molecular Biology, 2022.

Suggestion: The authors should add cohesin (RAD21/SMC1A) and NIPBL ChIP-seq for better interpretation. (2) Figure 3B: If delta2CBS only has heterozygenous deletion of CBS6, why we would expect the binding will be weaken to 50%. However, the CTCF binding is reduced to around 1/10 in the ChIP-qPCR. How do the authors explain this?

(3) Figure 3C: There are two problems with the 4C experiments: (a) The changes are really mild. In fact, none of the p-values in Figure 3D are significant; (b) The authors should also consider a model that CTCF directly serves as a repressor. In this way, 3D genome may not be involved. B-A switch is simply caused by the activation of the locus. 2. (CTCF) detachment: The authors mentioned few times "detachment". In the context of this manuscript, the authors indicate detachment from nuclear lamina. However, the authors haven't provide convincing evidence about this.

(1) Figure 1D: I doubt whether such changes of CTCF protein abundance will lead to LAD detachment. Suggest the authors read van Schaik et al., Genome Biology, 2022. With the full depletion of CTCF, the effects on LADs are still very restricted.

(2) Figure 2D: Lamin B1 should be mostly at nuclear periphery. I have few questions: (1) is the antibody specific? (2) do these cells carry mutation in LMNB1 gene? (3) is the staining actually LMNA? 3. Opposite functions of GATA4 and CTCF: These data in Figure 5E-H argues the opposite role of GATA4 and CTCF in transcriptional regulation. Would it be that CTCF KD just affected cell proliferation, which is actually known for many cell types, rather than affect CM differentiation process? If this is the reason, inversed correlation between CTCF KD and GATA4 KD in Figure 4D could also be explained by opposite effects on cell cycle. 4. In discussion, the authors suggested that CTCF is a local chromatin remodeller. In my view, association with local chromatin compaction doesn't qualify CTCF as a chromatin remodeler. To my knowledge, CTCF does not have an enzymatic domain, then how does it remodel chromatin? 5. Some conclusions are drawn based on insignificant p-values, e.g. Figure 2F, Figure 3D, etc. The authors should be careful about their conclusion, and tone down their statement for the observations have borderline significance.

Minor comments:

1. Figure 1A: (1) I suggest to label two promoters in the gene model. It's unclear in the figure in the current version; (2) I was a bit confused with the way how the authors labeled CTCF directionality. I thought there are a lot of promoters. Why didn't they use triangles?
2. Figure 2C: I think the drastical reduction of titin-mEGFP levels is only due to the way how the authors analyze their FACS data. Can the author quantify on median fluorescence intensity?
3. Figure S2G: P value should be -log10, I assume. Please label it accurately.

Significance

Strengths and limitations:

I feel that single-cell analysis and functional analysis of GATA4 and CTCF using cardiac organoid model are elegant. However, the weak part of the manuscript is the link between 3D genome and activation of TTN. I also think the authors should include more possible explanations for the interpretation of some genome organization data (CTCF site deletion, 4C, etc).

Advance: The study does provide useful information to understand transcriptional regulation during cardiac lineage specification. The link between 3D genome and cardiac lineage specification is conceptually nice but needs more data to support.

Audience: developmental biologists who is interested in heart development and molecular biologists with specific interests in gene regulation.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This report demonstrates that the gene expression output of the Wnt pathway, when controlled precisely by a synthetic light-based input, depends substantially on the frequency of stimulation. The particular frequency-dependent trend that is observed - anti-resonance, a suppression of target gene expression at intermediate frequencies given a constant duty cycle - is a novel aspect that has not been clearly shown before for this or other signaling pathways. The paper provides both clear experimental evidence of the phenomenon with engineered cellular systems and a model-based analysis of how the pairing of rate constants in pathway activation/deactivation could result in such a trend.

Strengths:

This report couples in vitro experimental data with an abstracted mathematical model. Both of these approaches appear to be technically sound and to provide consistent and strong support for the main conclusion. The experimental data are particularly clear, and the demonstration that Brachyury expression is subject to anti-resonance in ESCs is particularly compelling. The modeling approach is reasonably scaled for the system at the level of detail that is needed in this case, and the hidden variable analysis provides some insight into how the anti-resonance works.

Weaknesses:

(1) The anti-resonance phenomenon has not been demonstrated using physiological Wnt ligands; however, I view this as only a minor weakness for an initial report of the phenomenon. The potential significance of the phenomenon for Wnt outweighs the amount of effort it would take to carry the demonstration further - testing different frequencies/duty cycles at the level of ligand stimulus using microfluidics could get quite involved, and would likely take quite some time. Adding some more discussion about how the time scales of ligand-receptor binding could play into the reduced model would further ameliorate this issue.

We thank the reviewer for this comment and the interesting suggestion to test the anti-resonance phenomenon with microfluidics. We agree that combining physiological Wnt ligands with microfluidic stimulation would go beyond the scope of this current study, though it is an interesting extension. One advantage of the optogenetic setup, as mentioned in the discussion, is that the Wnt stimulus can be turned off sharply. This allows us to test the output from perfectly square wave input profiles; in microfluidics, washing the sticky ligand off the cells might “smear” the effective input profile cells respond to.

We show in Supplement Fig. 6, that our reduced model matches the experimental data and that we would expect the antiresonance phenomenon as long as (see Fig. 4). Practically, a smeared input profile implies an effective reduction of 𝑘_off, which means that the phenomenon would be visible with microfluidics (provided the minimum is deep enough, see Fig. 4). However, this should still be considered with caution, as the antiresonance would then appear because the cells essentially receive a smeared out or continuous pulse in the high frequency limit, rather than cells responding to a square wave in a specific way.

(2) While the model is fully consistent with the data, it has not been validated using experimental manipulations to establish that the mechanisms of the cell system and the model are the same. There may be some ways to make such modifications, for example, using a proteasome inhibitor. An alternative would be to more explicitly mention the need to validate the model's mechanism with experiments.

We thank the reviewer for this valuable and constructive comment. We agree that future experimental perturbations that directly modulate pathway activation and reset kinetics—such as proteasome inhibition, targeted degradation of pathway components, or engineered changes in receptor turnover—would provide an important validation of the model’s mechanistic interpretation. In the present study, our primary goal was to establish the existence and quantitative features of anti-resonance in the Wnt pathway and to identify the minimal set of timescale relationships that can explain it. We view the proposed experimental validations as exciting next steps that extend beyond the scope of the current work, and we are grateful to the reviewer for emphasizing their importance. We now mention this explicitly in the discussion of our manuscript.

(3) I think the manuscript misses an opportunity to discuss the potential of the phenomenon in other pathways. The hedgehog pathway, for example, involves GSK3-mediated partial proteolysis of a transcription factor, which could conceivably be subject to similar behaviors, and there are certainly other examples as well.

We thank the reviewer for pointing out an opportunity to emphasize the possibility of this phenomenon in other pathways. The minimal model indicates that anti-resonance emerges whenever a rapid activating process is paired with a slower deactivating/reset process. Beyond Hedgehog/Gli processing, candidate circuits include: NF-κB (rapid IκBα phosphorylation/degradation vs slower IκBα resynthesis), ERK (fast phosphorylation bursts vs slower transcriptional negative feedback such as DUSPs), Notch (fast γ-secretase NICD release vs slower NICD turnover and feedback), BMP/TGF-β–SMAD (fast R-SMAD phosphorylation vs slower receptor trafficking/SMAD7 feedback), and Hippo/YAP (rapid cytoplasmic sequestration vs slower transcriptional feedback). Each contains the same timescale separation that should create a frequency ‘stop-band,’ predicting suppressed gene expression or fate transitions at intermediate stimulation frequencies. We have updated the manuscript’s discussion to mention the Hedgehog connection with the following added sentence in the discussion: Analogous band-stop filtering should arise in other developmental circuits that couple a fast ‘ON’ step to slower deactivation or negative feedback. In Hedgehog, for example, PKA/CK1/GSK3-mediated partial proteolysis of Gli with slower recovery of full-length Gli creates the same fast-activation/slow-reset motif our hidden-variable model predicts will yield anti-resonance, and Wnt–Hedgehog crosstalk through the shared kinase GSK3 suggests such frequency selectivity could occur in other developmental signaling pathways.

We also added an additional sentence regarding different activation and deactivation timescales in other pathways.

(4) Some aspects of the modeling and hidden variable analysis are not optimally presented in the main text, although when considered together with the Supplemental Data, there are no significant deficiencies.

We have addressed the model choices and analysis now more clearly in the main manuscript and also referred to the Supplemental Data more directly.

Reviewer #2 (Public review):

Summary:

By combining optogenetics with theoretical modelling, the authors identify an anti-resonance behavior in the WnT signaling pathway. This behavior is manifested as a minimal response at a certain stimulation frequency. Using an abstracted hidden variable model, the authors explain their findings by a competition of timescales. Furthermore, they experimentally show that this anti-resonance influences the cell fate decision involved in human gastrulation.

Strengths:

(1) This interdisciplinary study combines precise optogenetic manipulation with advanced modelling.

(2) The results are directly tested in two different systems: HEK293T cells and H9 human embryonic stem cells.

(3) The model is implemented based on previous literature and has two levels of detail: i) a detailed biochemical model and ii) an abstract model with a hidden parameter.

Weaknesses:

(1) While the experiments provide both single-cell data and population data, the model only considers population data.

We thank the reviewer for correctly pointing out that the single-cell measurements would in principle allow us to incorporate the cell-to-cell heterogeneity into the model. In this study, we sought to identify a minimal quantitative model of the Wnt pathway that could explain anti-resonance through competing time scales. We believe that, for our purposes, focusing on population data allowed us to keep the complexity of the model to a minimum to increase its explanatory value. We agree with the reviewer that considering single-cell trajectories is an interesting direction for further work.

(2) Although the model captures the experimental data for TopFlash very well, the beta-Cat curves (Figure 2B) are only described qualitatively. This discrepancy is not discussed.

Indeed, our model fits to mean β-catenin expressions are more qualitative than for TopFlash. The fit for β-catenin was tricky, as expression of β-catenin is typically low and closer to the detectable limits than TopFlash. These experimental constraints mean that the variation between individual signal trajectories is higher for β-catenin compared to the light-off condition than for TopFlash. Therefore, we strove to obtain a qualitative rather than a quantitative fit to the mean expression profile in β-catenin.  The current model fit is well within the standard deviation of variation. Given the observed heterogeneity and the fact that we take the parameters from literature (which ensures that the order of magnitude of parameters is in a sensible range), we believe that the model fits are reasonable. We now mention this explicitly in the text.

Overall Assessment:

The authors convincingly identified an anti-resonance behavior in a signaling pathway that is involved in cell fate decisions. The focus on a dynamic signal and the identification of such a behavior is important. I believe that the model approach of abstracting a complicated pathway with a hidden variable is an important tool to obtain an intuitive understanding of complicated dependencies in biology. Such a combination of precise ontogenetic manipulation with effective models will provide a new perspective on causal dependencies in signaling pathways and should not be limited only to the system that the authors study.

We thank both reviewers for the positive assessment of our manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

There are several points that deserve more discussion, as noted above in the review.

(1) It would be worthwhile to consider whether a relatively simple experiment with a proteasome inhibitor or similar pharmacological manipulation could provide useful validation data for the model.

We address this point above in the weaknesses section from reviewer 1.

(2) The figure legend for S5C should clarify whether the values plotted are at a particular fixed time point, or (more likely) at a certain time following the second pulse, which would be variable.

We have modified the figure caption to clarify that the values plotted are at a fixed time point in the simulation (t\=48 hrs). We chose this timepoint sufficiently long after the second pulse to ensure that there are no residual dynamical effects. We thank the reviewer for noting this.

(3) As noted in the Sci Score document, various aspects of the resource reporter should be improved, such as including RRIDs, etc.

We are sending out our plasmids to AddGene; versions for Python and Matlab are listed in our methods section.

Reviewer #2 (Recommendations for the authors):

I mostly have suggestions to improve the clarity of the presentation.

(1) Not all symbols in the equations given in the main text are explained. This is rather annoying, because either you present them and explain what they are or you don't show them and refer to the supplements. For example, d_0 or c_o or \bar{b} or n or K are not explained.

We have now more clearly presented the parameters in the main text and added signposts to the Methods section.

(2) Overall, it is often not clear what data in the figures are redundant, although the authors referred to them in the text. For example, in Figure 2c, a curve for 24 hours is shown and referred back to Figure 1D. However, in Figure 1D there is no curve for 24 hours. Is the data from Supplementary Figure 1 H and K also in the main text?

We thank the referee for pointing out these redundancies. We have now included the 24hr line in Figure 1D and are now only showing the unsmoothed data, also in the main text of the manuscript. To clarify supplemental figures, we have now removed S1H and S1K since all they showed was the unsmoothed version of the data. The remaining plots in Supplementary Figure 1 are normalized differently from what we show in Figure 1 to demonstrate our choice of normalization is not the reason for the observed optogenetic response.

Author response:

Reviewer #1 (Public Review):

Lai and Doe address the integration of spatial information with temporal patterning and genes that specify cell fate. They identify the Forkhead transcription factor Fd4 as a lineage-restricted cell fate regulator that bridges transient spatial transcription factors to terminal selector genes in the developing Drosophila ventral nerve cord. The experimental evidence convincingly demonstrates that Fd4 is both necessary for lateborn NB7-1 neurons, but also sufficient to transform other neural stem cell lineages toward the NB7-1 identity. This work addresses an important question that will be of interest to developmental neurobiologists: How can cell identities defined by initial transient developmental cues be maintained in the progeny cells, even if the molecular mechanism remains to be investigated? In addition, the study proposes a broader concept of lineage identity genes that could be utilized in other lineages and regions in the Drosophila nervous system and in other species. 

Thanks for the accurate summary and positive comments!

While the spatial factors patterning the neuroepithelium to define the neuroblast lineages in the Drosophila ventral nerve cord are known, these factors are sometimes absent or not required during neurogenesis. In the current work, Lai and Doe identified Fd4 in the NB7-1 lineage that bridges this gap and explains how NB7-1 neurons are specified after Engrailed (En) and Vnd cease their expression. They show that Fd4 is transiently co-expressed with En and Vnd and is present in all nascent NB7-1 progenies. They further demonstrate that Fd4 is required for later-born NB7-1 progenies and sufficient for the induction of NB7-1 markers (Eve and Dbx) while repressing markers of other lineages when force-expressed in neural progenitors, e.g., in the NB56 lineage and in the NB7-3 lineage. They also demonstrate that, when Fd4 is ectopically expressed in NB7-3 and NB5-6 lineages, this leads to the ectopic generation of dorsal muscle-innervating neurons. The inclusion of functional validation using axon projections demonstrates that the transformed neurons acquire appropriate NB7-1 characteristics beyond just molecular markers. Quantitative analyses are thorough and well-presented for all experiments.

Thanks for the positive comments!

(1) While Fd4 is required and sufficient for several later-born NB7-1 progeny features, a comparison between early-born (Hb/Eve) and later-born (Run/Eve) appears missing for pan-progenitor gain of Fd4 (with sca-Gal4; Figure 4) and for the NB7-3 lineage (Figure 6). Having a quantification for both could make it clearer whether Fd4 preferentially induces later-born neurons or is sufficient for NB7-1 features without temporal restriction.

We quantified the percentage of Hb+ and Runt+ cells among Eve+ cells with sca-gal4, and the results are shown in Figure 4-figure supplement 1. We found that the proportion of early-born cells is slightly reduced but the proportion of later-born cells remain similar. Interestingly, we also found a subset of Eve+ cells with a mixed fate (Hb+Runt+) but the reason remains unclear.

(2) Fd4 and Fd5 are shown to be partially redundant, as Fd4 loss of function alone does not alter the number of Eve+ and Dbx+ neurons. This information is critical and should be included in Figure 3.

Because every hemisegment in an fd4 single mutant is normal, we just added it as the following text: “In fd4 mutants, we observe no change in the number of Eve+ neurons or Dbx+ neurons (n=40 hemisegments).”

(3) Several observations suggest that lineage identity maintenance involves both Fd4dependent and Fd4-independent mechanisms. In particular, the fact that fd4-Gal4 reporter remains active in fd4/fd5 mutants even after Vnd and En disappear indicates that Fd4's own expression, a key feature of NB7-1 identity, is maintained independently of Fd4 protein. This raises questions about what proportion of lineage identity features require Fd4 versus other maintenance mechanisms, which deserves discussion.

We agree, thanks for raising this point. We add the following text to the Discussion. “Interestingly, the fd4 fd5 mutant maintains expression of fd4:gal4, suggesting that the fd4/fd5 locus may have established a chromatin state that allows “permanent” expression in the absence of Vnd, En, and Fd4/Fd5 proteins.”

(4) Similarly, while gain of Fd4 induces NB7-1 lineage markers and dorsal muscle innervation in NB5-6 and NB7-3 lineages, drivers for the two lineages remain active despite the loss of molecular markers, indicating some regulatory elements retain activity consistent with their original lineage identity. It is therefore important to understand the degree of functional conversion in the gain-of-function experiments. Sparse labeling of Fd4 overexpressing NB5-6 and NB7-3 progenies, as was done in Seroka and Doe (2019), would be an option.

We agree it is interesting that the NB7-3 and NB5-6 drivers remain on following Fd4 misexpression. To explore this, we used sca-gal4 to overexpress Fd4 and observed that Lbe expression persisted while Eg was largely repressed (see Author response image 1 below). The results show that Lbe and Eg respond differently to Fd4. A non-mutually exclusive possibility is that the continued expression of lbe-Gal4 UAS-GFP or eg-Gal4 UAS-GFP may be due to the lengthy perdurance of both Gal4 and GFP.

Author response image 1.

(5) The less-penetrant induction of Dbx+ neurons in NB5-6 with Fd4-overexpression is interesting. It might be worth the authors discussing whether it is an Fd4 feature or an NB56 feature by examining Dbx+ neuron number in NB7-3 with Fd4-overexpression.

In the NB7-3 lineages misexpressing Fd4, only 5 lineages generated Dbx+ cells (0.1±0.4, n=64 hemisegments), suggesting that the low penetrance of Dbx+ induction is an intrinsic feature of Fd4 rather than lineage context. We have added this information in the results section. 

(6) It is logical to hypothesize that spatial factors specify early-born neurons directly, so only late-born neurons require Fd4, but it was not tested. The model would be strengthened by examining whether Fd4-Gal4-driven Vnd rescues the generation of laterborn neurons in fd4/fd5 mutants.

When we used en-gal4 driver to express UAS-vnd in the fd4/fd5 mutant background, we found an average 7.4±2.2 Eve+ cells per hemisegment (n=36), significantly higher than fd4/fd5 mutant alone (3.9±0.8 cells, n=52, p=2.6x10<sup.-11</sup>) (Figure 3J). In addition, 0.2±0.5 Eve+ cells were ectopic Hb+ (excluding U1/U2), indicating that Vnd-En integration is sufficient to generate both early-born and late-born Eve+ cells in the fd4/fd5 mutants. We have added the results to the text.

(7) It is mentioned that Fd5 is not sufficient for the NB7-1 lineage identity. The observation is intriguing in how similar regulators serve distinct roles, but the data are not shown. The analysis in Figure 4 should be performed for Fd5 as supplemental information.

Thanks for the suggestion. Because the results are exactly the same as the wild type, we don’t think it is necessary to provide an additional images or analysis as supplemental information.

Reviewer #2 (Public review):

Via a detailed expression analysis, they find that Fd4 is selectively expressed in embryonic NB7-1 and newly born neurons within this lineage. They also undertake a comprehensive genetic analysis to provide evidence that fd4 is necessary and sufficient for the identity of NB7-1 progeny. 

Thanks for the accurate summary!

The analysis is both careful and rigorous, and the findings are of interest to developmental neurobiologists interested in molecular mechanisms underlying the generation of neuronal diversity. Great care was taken to make the figures clear and accessible. This work takes great advantage of years of painstaking descriptive work that has mapped embryonic neuroblast lineages in Drosophila. 

Thanks for the positive comments!

The argument that Fd4 is necessary for NB7-1 lineage identity is based on a Fd4/Fd5 double mutant. Loss of fd4 alone did not alter the number of NB7-1-derived Eve+ or Dbx+ neurons. The authors clearly demonstrate redundancy between fd4 and fd5, and the fact that the LOF analysis is based on a double mutant should be better woven through the text.

The authors generated an Fd5 mutant. I assume that Fd5 single mutants do not display NB7-1 lineage defects, but this is not stated. The focus on Fd4 over Fd5 is based on its highly specific expression profile and the dramatic misexpression phenotypes. But the LOF analysis demonstrates redundancy, and the conclusions in the abstract and through the results should reflect the existence of Fd5 in the conclusions of this manuscript.

We agree, and have added new text to clarify the single mutant phenotypes (there are none) and the double mutant phenotype (loss of NB7-1 molecular and morphological features. The following text is added to the manuscript: “Not surprisingly, we found that fd4 single mutants or fd5 single mutants had no phenotype (Eve+ neurons were all normal). Thus, to assess their roles, we generated a fd4 and fd5 double mutant. Because many Eve+ and Dbx+ cells are generated outside of NB7-1 lineage, it was also essential to identify the Eve+ or Dbx+ cells within NB7-1 lineage in wild type and fd4 mutant embryos. To achieve this, we replaced the open reading frame of fd4 with gal4 (called fd4-gal4) (see Methods); this stock simultaneously knocked out both fd4 and fd5 (called fd4/fd5 mutant hereafter) while specifically labeling the NB7-1 lineage. For the remainder of this paper we use the fd4/fd5 double mutant to assay for loss of function phenotypes.”

It is notable that Fd4 overexpression can rewire motor circuits. This analysis adds another dimension to the changes in transcription factor expression and, importantly, demonstrates functional consequences. Could the authors test whether U4 and U5 motor axon targeting changes in the fd4/fd5 double mutant? To strengthen claims regarding the importance of fd4/fd5 for lineage identity, it would help to address terminal features of U motorneuron identity in the LOF condition.

Thanks for raising this important point. We examined the axon targeting on body wall muscles in both wild type and in fd4/fd5 mutant background and added the results in Figure 3-figure supplement 2. We found that the axon targeting in the late-born neuron region (LL1) is significantly reduced, suggesting that the loss of late-born neurons in fd4/fd5 mutant leads to the absence of innervation of corresponding muscle targets.

Reviewer #3 (Public review):

The goal of the work is to establish the linkage between the spatial transcription factors (STFs) that function transiently to establish the identities of the individual NBs and the terminal selector genes (typically homeodomain genes) that appear in the newborn postmitotic neurons. How is the identity of the NB maintained and carried forward after the spatial genes have faded away? Focusing on a single neuroblast (NB 7-1), the authors present evidence that the fork-head transcription factor, fd4, provides a bridge linking the transient spatial cues that initially specified neuroblast identity with the terminal selector genes that establish and maintain the identity of the stem cell's progeny. 

Thanks for the positive comments!

The study is systematic, concise, and takes full advantage of 40+ years of work on the molecular players that establish neuronal identities in the Drosophila CNS. In the embryonic VNC, fd4 is expressed only in the NB 7-1 and its lineage. They show that Fd4 appears in the NB while the latter is still expressing the Spatial Transcription Factors and continues after the expression of the latter fades out. Fd4 is maintained through the early life of the neuronal progeny but then declines as the neurons turn on their terminal selector genes. Hence, fd4 expression is compatible with it being a bridging factor between the two sets of genes. 

Thanks for the accurate summary!

Experimental support for the "bridging" role of Fd4 comes from a set of loss-of-function and gain-of-function manipulations. The loss of function of Fd4, and the partially redundant gene Fd5, from lineage 7-1 does not aoect the size of the lineage, but terminal markers of late-born neuronal phenotypes, like Eve and Dbx, are reduced or missing. By contrast, ectopic expression of fd4, but not fd5, results in ectopic expression of the terminal markers eve and Dbx throughout diverse VNC lineages. 

Thanks for the accurate summary!

A detailed test of fd4's expression was then carried out using lineages 7-3 and 5-6, two well-characterized lineages in Drosophila. Lineage 7-3 is much smaller than 7-1 and continues to be so when subjected to fd4 misexpression. However, under the influence of ectopic Fd4 expression, the lineage 7-3 neurons lost their expected serotonin and corazonin expression and showed Eve expression as well as motoneuron phenotypes that partially mimic the U motoneurons of lineage 7-1.

Thanks for the positive comments!

Ectopic expression of Fd4 also produced changes in the 5-6 lineage. Expression of apterous, a feature of lineage 5-6, was suppressed, and expression of the 7-1 marker, Eve, was evident. Dbx expression was also evident in the transformed 5-6 lineages, but extremely restricted as compared to a normal 7-1 lineage. Considering the partial redundancy of fd4 and fd5, it would have been interesting to express both genes in the 5-6 lineage. The anatomical changes that are exhibited by motoneurons in response to Fd4 expression confirm that these cells do, indeed, show a shift in their cellular identity.

We appreciate the positive comments. We agree double misexpression of Fd4 and Fd5 might give a stronger phenotype (as the reviewer says) but the lack of this experiment does not change the conclusions that Fd4 can promote NB7-1 molecular and morphological aspects at the expense of NB5-6 molecular markers.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

The study introduces an open-source, cost-effective method for automating the quantification of male social behaviors in Drosophila melanogaster. It combines machine-learning-based behavioral classifiers developed using JAABA (Janelia Automatic Animal Behavior Annotator) with inexpensive hardware constructed from off-the-shelf components. This approach addresses the limitations of existing methods, which often require expensive hardware and specialized setups. The authors demonstrate that their new "DANCE" classifiers accurately identify aggression (lunges) and courtship behaviors (wing extension, following, circling, attempted copulation, and copulation), closely matching manually annotated groundtruth data. Furthermore, DANCE classifiers outperform existing rule-based methods in accuracy. Finally, the study shows that DANCE classifiers perform as well when used with low-cost experimental hardware as with standard experimental setups across multiple paradigms, including RNAi knockdown of the neuropeptide Dsk and optogenetic silencing of dopaminergic neurons.

The authors make creative use of existing resources and technology to develop an inexpensive, flexible, and robust experimental tool for the quantitative analysis of Drosophila behavior. A key strength of this work is the thorough benchmarking of both the behavioral classifiers and the experimental hardware against existing methods. In particular, the direct comparison of their low-cost experimental system with established systems across different experimental paradigms is compelling.

While JAABA-based classifiers have been previously used to analyze aggression and courtship (Tao et al., J. Neurosci., 2024; Sten et al., Cell, 2023; Chiu et al., Cell, 2021; Isshi et al., eLife, 2020; Duistermars et al., Neuron, 2018), the demonstration that they work as well without expensive experimental hardware opens the door to more low-cost systems for quantitative behavior analysis.

We thank the reviewer for their positive assessment and constructive suggestions. We have cited these additional JAABA studies in the Introduction. We clarified that several prior JAABA-based classifiers were developed using specialized machinevision cameras or custom setups, and that in some cases the original code and classifiers were not made publicly available, which limits reproducibility and wider adoption. To address this, we explicitly note in the revised manuscript that DANCE was developed with accessibility in mind.

Although the study provides a detailed evaluation of DANCE classifier performance, its conclusions would be strengthened by a more comprehensive analysis. The authors assess classifier accuracy using a bout-level comparison rather than a frame-level analysis, as employed in previous studies (Kabra et al., Nat Methods, 2013). They define a true positive as any instance where a DANCE-detected bout overlaps with a manually annotated ground-truth bout by at least one frame. This criterion may inflate true positive rates and underestimate false positives, particularly for longer-duration courtship behaviors. For example, a 15-second DANCE-classified wing extension bout that overlaps with ground truth for only one frame would still be considered a true positive. A frame-level analysis performance would help address this possibility.

We thank the reviewer for raising this important point. Our original use of bout-level analysis followed existing literature (Duistermars et al., 2018; Ishii et al., 2020; Chiu et al., 2021; Tao et al., 2024; Hindmarsh Sten et al., 2025). While our lunge classifier already operates at the frame level, we have now performed additional frame-level evaluations for the duration based courtship classifiers. These analyses revealed only minor differences in precision, recall, and F1 scores compared with the original bout-level approach (see new Figure 5—Figure Supplement 3). Details of this analysis are now included in the Materials and Methods.

In summary, this work provides a practical and accessible approach to quantifying Drosophila behavior, reducing the economic barriers to the study of the neural and molecular mechanisms underlying social behavior.

We thank the reviewer for their encouraging comments and for recognizing the accessibility and practical value of our approach. We appreciate the constructive suggestions, which have helped strengthen the manuscript.

Reviewer #2 (Public review):

Summary:

This manuscript addresses the development of a low-cost behavioural setup and standardised open-source high-performing classifiers for aggression and courtship behaviour. It does so by using readily available laboratory equipment and previously developed software packages. By comparing the performance of the setup and the classifiers to previously developed ones, this study shows the classifier's overperformance and the reliability of the low-cost setup in recapitulating previously described effects of different manipulations on aggression and courtship.

Strengths:

The newly developed classifiers for lunges, wing extension, attempted copulation, copulation, following, and circling, perform better than available previously developed ones. The behavioural setup developed is low cost and reliably allows analysis of both aggression and courtship behaviour, validated through social experience manipulation (social isolation), gene knock (Dsk in Dilp2 neurons) and neuronal inactivation (dopaminergic neurons) known to affect courtship and aggression.

We thank the reviewer for the clear summary of our work and for highlighting its strengths. We appreciate these positive comments and suggestions, which have helped improve the clarity of the manuscript.

Weaknesses:

Aggression encompasses multiple defined behaviours, yet only lunges were analysed. Moreover, the CADABRA software to which DANCE was compared analyses further aggression behaviours, making their comparisons incomplete. In addition, though DANCE performs better than CADABRA and Divider in classifying lunges in the behavioural setup tested, it did not yield very high recall and F1 scores.

We thank the reviewer for raising this important point. We focused on lunges because they are widely used as a standard proxy for male aggression across multiple laboratories (Agrawal et al., 2020; Asahina et al., 2014; Chiu et al., 2021; Chowdhury et al., 2021; Dierick et al., 2007; Hoyer et al., 2008; Jung et al., 2020; Nilsen et al., 2004; Watanabe et al., 2017). As noted in the Discussion, our study also provides a template for the future development of additional aggression classifiers (fencing, wing flick, tussle, chase, female headbutt) and courtship classifiers (tapping, licking, rejection), which can be trained and shared through the same DANCE framework. Developing and validating these was beyond the scope of the present work.

To address the concern regarding precision, recall, and F1 scores, we performed additional analyses across all training videos and compiled these results in the new Figure 2—Figure Supplement 2. Our earlier lunge classifier had performance metrics obtained after training on a total of 11 videos. Our analysis shows performance metrics for classifiers trained on four independent datasets (Videos 8– 11). We found that the classifier trained on nine videos provided the best balance of precision, recall, and F1 (78.73%, 73.07%, and 75.79%, respectively), which was slightly better than the earlier classifier. We therefore updated the main figure, text, and Materials and Methods to use this version and uploaded the corresponding classifier and training details to the GitHub repository. 

DANCE is of limited use for neuronal circuit-level enquiries, since mechanisms for intensity and temporally controlled optogenetic manipulations, which are nowadays possible with open-source software and low-cost hardware, were not embedded in its development.

We thank the reviewer for this valuable point. The primary aim of DANCE is to provide an accessible, modular, and low-cost behavioural recording and analysis platform. It was designed so that users can readily integrate additional components such as optogenetic control when needed. As a proof of concept, we implemented optogenetic silencing of dopaminergic neurons using the DANCE hardware and confirmed that this manipulation increased aggression (Figure 7R). 

To facilitate adoption, we now provide schematic diagrams, LED control code, and instructions on our GitHub page and setup photographs in the manuscript (see new Figure 7—Figure Supplement 1). The released code allows programmable timing and intensity control, enabling users to reproduce temporally precise optogenetic protocols or extend the system for other stimulation paradigms.

Reviewer #3 (Public review):

The preprint by Yadav et al. describes a new setup to quantify a number of aggression and mating behaviors in Drosophila melanogaster. The investigation of these behaviors requires the analysis of a large number of videos to identify each kind of behavior displayed by a fly. Several approaches to automatize this process have been published before, but each of them has its limitations. The authors set out to develop a new setup that includes very low-cost, easy-to-acquire hardware and open-source machine-learning classifiers to identify and quantify the behavior.

Strengths:

(1) The study demonstrates that their cheap, simple, and easy-to-obtain hardware works just as well as custom-made, specialized hardware for analyzing aggression and mating behavior. This enables the setup to be used in a wide range of settings, from research with limited resources to classroom teaching.

(2) The authors used previously published software to train new classifiers for detecting a range of behaviors related to aggression and mating and to make them freely available. The classifiers are very positively benchmarked against a manually acquired ground truth as well as existing algorithms.

(3) The study demonstrates the applicability of the setup (hardware and classifiers) to common methods in the field by confirming a number of expected phenotypes with their setup.

We thank the reviewer for the positive assessment of our work and for highlighting its strengths. We appreciate these encouraging comments and suggestions, which have helped improve the clarity and presentation of the manuscript.

Weaknesses:

(1) When measuring the performance of the duration-based classifiers, the authors count any bout of behavior as true positive if it overlaps with a ground-truth positive for only 1 frame - despite the minimal duration of a bout is 10 frames, and most bouts are much longer. That way, true positives could contain cases that are almost totally wrong as long there was an overlap of a single frame. For the mating behaviors that are classified in ongoing bouts, I think performance should be evaluated based on the % of correctly classified frames, not bouts.

We thank the reviewer for raising this concern. In response to this point, and to Reviewer #1’s similar comment, we performed a frame-level evaluation of all duration-based courtship classifiers. The analysis revealed only minor differences compared with the original bout-level metrics (see new Figure 5—Figure Supplement 3), confirming the robustness of our classifiers. We have also added a description of this analysis in the Materials and Methods section.

(2) In the methods part, only one of the pre-existing algorithms (MateBook), is described. Given that the comparison with those algorithms is a so central part of the manuscript, each of them should be briefly explained and the settings used in this study should be described.

We thank the reviewer for this helpful suggestion. In the revised manuscript, we expanded the Materials and Methods to include concise descriptions and parameter settings for all pre-existing algorithms used for comparison. This includes dedicated subsections for CADABRA and the Divider assay, with explicit reference to their rulebased or geometric features. For MateBook, we specified the persistence filters used and the adjustments made for fair benchmarking. These changes ensure transparency and reproducibility.

Taken together, this work can greatly facilitate research on aggression and mating in Drosophila. The combination of low-cost, off-the-shelf hardware and open-source, robust software enables researchers with very little funding or technical expertise to contribute to the scientific process and also allows large-scale experiments, for example in classroom teaching with many students, or for systematic screenings.

We thank the reviewer for the encouraging comments and for recognizing the accessibility and broad applicability of DANCE. We believe these revisions have further strengthened the manuscript.

Reviewer #1 (Recommendations for the authors):

The following comments highlight areas where additional context, clarification, or further analysis could strengthen the manuscript. I hope these suggestions will be useful in refining your work.

(1) Lines 71-73: The authors state that Ctrax "leads to frequent identity switches among tracked flies, which is not the case while using FlyTracker." However, Ctrax was specifically designed to minimize identity errors, and Kabra et al. (2013) reported a low frequency of such errors-approximately one per five fly-hours in 10-fly videos. In contrast, Caltech FlyTracker does not correct identity errors automatically, requiring manual corrections, as noted in the Methods section of this study. If this is not an oversight, please provide further context to clarify this distinction.

We thank the reviewer for raising this clarification. As reported by Bentzur et al. (2021), when groups of flies were tracked simultaneously, Ctrax often generated multiple identities for the same individual, sometimes producing more trajectories than the actual number of flies. To prevent ambiguity, we revised the text to read: “While both Ctrax and FlyTracker (Eyjolfsdottir et al., 2014) may produce identity switches, when groups of flies were tracked simultaneously, Ctrax led to inaccuracies that required manual correction using specialized algorithms such as FixTrax (Bentzur et al., 2021).”  We also quantified FlyTracker identity-switch rates in our datasets and report them in new Supplementary File 5, confirming that such events were rare (< 2% of tracked intervals). We believe, this updated version provides the necessary context and ensures accuracy in describing each tracker’s limitations.

(2) Line 85: Providing additional context on how this study builds on previous work using JAABA-based classifiers for fly social behavior and comparing these classifiers to rule-based methods would more accurately situate it within the field. The authors state that "recently, a few JAABA-based classifiers have been developed for measuring aggression and courtship" and cite four related studies. However, this statement seems to underrepresent the use of JAABA-based classifiers for quantifying fly social behavior, which has become common in the field. Several additional studies (as noted in the public review) have developed JAABA-based classifiers for scoring aggression or courtship. Furthermore, other studies have compared the performance of JAABA-based classifiers with rule-based classifiers like CADABRA (e.g., Chowdhury et al., Comm Biology 2021; Leng et al., PlosOne 2020; Kabra et al., Nat Methods 2013). Mentioning the similar findings in those studies and your own helps strengthen the conclusion that machine-learning-based classifiers outperform rule-based classifiers in several experimental contexts.

We thank the reviewer for this helpful suggestion. We have revised the Introduction to include additional references to studies that applied JAABA-based classifiers for aggression and courtship and made textual edits to reflect this. We further noted that, unlike several previous studies, all DANCE classifiers and analysis code are publicly available.

Reviewer #2 (Recommendations for the authors):

(1) Suggestions for improved or additional experiments, data or analyses: As mentioned in the description of the effect of optogenetic inactivation of dopaminergic neurons, in the conclusion and also reported in the literature, there are other important identified aggression behaviours, such as fencing, wing flick, tussle, and chase. Similarly, for courtship, tapping and licking have also been defined. This study, as opposed to proposed future studies, would benefit from creating opensource classifiers for these established behaviours, which are important for the analysis of aggression and courtship.

We thank the reviewer for this valuable suggestion. As clarified in the Discussion, this manuscript intentionally focuses on six core, well-validated aggression and courtship behaviors to demonstrate DANCE’s modularity and reproducibility. Developing additional classifiers such as fencing, wing flick, tussle, chase, tapping, and licking would require extensive annotation and validation beyond the present scope. To address this point, we explicitly note in the revised text that the DANCE pipeline is readily extendable, allowing the community to build new classifiers within the same framework.

In terms of observer bias assessment for ground-truthing in courtship, this was only presented for circling and it would be beneficial to have encompassed all behaviours analysed.

We thank the reviewer for this suggestion. Observer-bias comparisons for all six classifiers are presented in Figure 2—Figure Supplement 1 (panels A–F). We clarified in the Results that annotations from two independent evaluators were compared for all classifiers, with no significant differences observed, confirming their robustness.

Finally, intensity and temporal optogenetic control are important for neuronal circuit analysis of underlying behaviour. The authors could embed this aspect in DANCE by integrating control of the green light LED strip used in this study using, for example, the open-source visual reactive programming software Bonsai (Lopes et al., 2015) and open-source electronics platform Arduino. This is an important and valuable addition in line with maintaining low cost.

We thank the reviewer for this valuable suggestion. DANCE was designed to be modular, allowing integration of temporal optogenetic control. To support immediate adoption, we now provide Arduino LED control code, setup schematics, and photographs (new Figure 7—Figure Supplement 1) along with step-by-step instructions on our GitHub page. We also note that Bonsai and Arduino frameworks are compatible with DANCE, enabling future extensions for closed-loop or behaviortriggered stimulation.

(2) Minor corrections to the text and figures:

Figure Supplement 1 refers only to Figure 2, yet panels D-F refer to the behaviour circling in courtship and therefore should be assigned to the respective figure.

Thanks, we have corrected this.

In lines 315-316, the cumbersome task of fluon coating for aggression assays seems to be ubiquitous across assays which is not the case, and therefore the sentence should include the word 'some'.

Thanks, we have edited this.

The cost of the phone and/or tablet should be included in the DANCE setup costs, as presumably these devices will be dedicated to the behavioural studies, for consistency purposes.

We thank the reviewer for this comment. We intentionally did not include smartphones or tablets in the setup cost because, in our experiments, these devices were not dedicated exclusively to DANCE but were repurposed from routine personal use. Our aim was to leverage readily available consumer electronics so that their cost does not become a barrier to adoption. We confirmed that commonly available Android phones capable of 30 fps at 1080p in H.264 format, as well as tablets or phones running a simple white-screen light app, are sufficient for reliable behavior classification and illumination. Since these devices can be returned to regular use after recordings, including their cost in the setup would not accurately reflect the intended accessibility of DANCE. For consistency, we now clarify in the Materials and Methods that such devices should be placed in airplane mode during recordings.

Reviewer #3 (Recommendations for the authors):

(1) For my taste, the authors put too much emphasis on the point that their method outperforms existing methods. I understand the value in comparing to published methods and it is of course fully justified to state the advantages of the new method. But the whole preprint is set up as a competition with the old algorithms, and the conclusion that the new classifier is better is repeated in each figure caption and after each paragraph of the results. This competitive mindset also extends to the selection of which results are presented as main figures and which as supplements - all cases in which the previous methods actually perform well are only presented in the supplement. I think this is simply unnecessary as the authors' results speak for themselves, and do not need the continuous competitive comparison.

We thank the reviewer for this thoughtful suggestion. Our intention was to benchmark DANCE rigorously against existing methods, not to frame the study competitively. We agree that repeated emphasis on relative performance was unnecessary. In the revised version, we streamlined figure captions and text throughout the manuscript to balance comparisons and removed redundant phrasing. Instances where other methods performed well are now presented with equal clarity to maintain a neutral and informative tone.

(2) When describing the DANCE hardware, as a reader I would find it interesting to also read about potential issues that the authors encountered. For example, how difficult is it to handle the materials without breaking or deforming them, which could affect the behavioral assays? How critical is it to use specific blister packs - the availability of which will likely vary strongly between countries? Did the authors try different sizes, and products? Such information, even as a supplement, could be very helpful for the widespread use of the hardware.

We thank the reviewer for this important point. To address this, we conducted additional tests comparing DANCE arenas of different diameters (new Figure 7— Figure Supplement 3A–C and new Figure 7—Figure Supplement 4A–L). We also consulted colleagues in multiple countries and verified that the blister packs used in our assays are readily available. The Materials and Methods now include practical handling notes: blister foils can be reused ~30–40 times for aggression assays and ~10–15 times for courtship assays before deformation. We also describe how to prevent agar surface damage during assembly and how to wash and dry the arenas for optimal reusability.

(3) I find the arrows pointing to several videos in a number of figures rather distracting and redundant, and suggest omitting them.

Thanks, we have omitted these arrows from all relevant figures and clarified the figure legends to enhance readability.

(4) P8, line 169 ff: this is a very long sentence that should be separated into several sentences.

We have rewritten this as follows: “DANCE scores remained comparable to groundtruth scores across all categories, whereas CADABRA and Divider underestimated the lunge counts (Figure 2B–E). Correlation analysis revealed a strong relationship between DANCE and ground-truth scores (Figure 2F, Supplementary File 2). In comparison, CADABRA and the Divider assay classifier showed a weaker correlation (Figure 2G-H, Supplementary File 2).”

(5) P10, line 216: please explain, here and in the methods, how these behavioral indices are calculated. I did not find this information anywhere in the paper.

We thank the reviewer for pointing this out. We now define the behavioral index explicitly in Materials and Methods: “For each assay, a behavioral index was calculated as the proportion of frames in which the male engaged in the specified behavior. This was obtained by dividing the total number of frames annotated for that behavior by the total number of frames in the recording.”

(6) P11, line 253: I don't understand the modifications to MateBook regarding attempted copulations, neither in the results nor the methods section. I would ask the authors to explain more explicitly what was done.

We thank the reviewer for this helpful suggestion. We have re-written several parts of the Materials and methods to clarify these details and streamline the text. To train the attempted copulation classifier, we combined datasets from assays with mated and decapitated virgin females, using manual annotations as ground truth. We also adapted MateBook’s persistence filters (Ribeiro et al., 2018) and defined thresholds explicitly: mounting lasting >45 s (>1350 frames at 30 fps) was defined as copulation, whereas abdominal curling without mounting, or mounting lasting 0.33– 45 s, was defined as attempted copulation.

(7) Figure 7F: this is the only case with a significant difference between the two setups. What explanations do the authors have for the discrepancy?

We thank the reviewer for raising this point. After repeating the experiments, we no longer found a significant difference between the setups. Figure 7 and its legend have been updated to reflect these results.

(8) Figure 2 - Supplement 1: I do not understand why the boxes for Observer 1 have different colors in different figures. Does this have a meaning?

Thanks for pointing this out. The color differences had no intended meaning, and we have corrected the figure for consistency across panels.

(9) P22, line 517ff: It would be interesting to know how frequently identity switches occurred. For large-scale, automatic behavioral screenings that step could be a crucial bottleneck.

We thank the reviewer for this valuable suggestion. We analyzed identity switches using the FlyTracker “Visualizer” package, which flags frames with possible overlaps or jumps. Flagged intervals were manually verified, and we report these data in new Supplementary File 5. Identity switch rates were very low: 0.66% for high-resolution recordings and 1.9% for smartphone DANCE videos in the most challenging decapitated-virgin dataset. These findings demonstrate robust tracking performance under both setups.

This passage really made me think. A lot of the time, when we learn about Indigenous people, we often hear about how they were oppressed, and it focuses on their suffering, but it hardly ever mentions their strength to stand tall despite the oppression they face every single day. I think it's important for both facts to coexist.

As the text mentions, things like social justice aren't always upheld. This is because, inherently, the structures in Western society benefit White colonizers the most. This raises the question of, "What can we do to change the structure that oppresses Indigenous people and people of colour?"

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Reply to the reviewers

Reviewer #1

1. First, the authors have not convincingly shown that skin cells, or more specifically skin ECs, are a major source of circulating G-CSF in the psoriasis model as stated in the title and abstract. The data in Figure 4 show selective upregulation of Csf3 gene in skin ECs and their ability to secrete G-CSF upon IMQ treatment in vitro. However, the provided data do not address to what degree the skin EC-derived G-CSF contributes to the elevated level of circulating G-CSF. Additional experiments to selectively deplete G-CSF in skin ECs, or at least in skin cells of the affected site, are warranted to support the authors' claim. Does intradermal injection of G-CSF neutralizing antibody into the psoriatic skin reduce circulating levels of G-CSF?

Author's response:

Thank you for reviewer's comment. We agree with the Reviewer#1 that it is important to directly block G-CSF to the skin via intradermal injection and measure the G-CSF level in the serum afterwards. Therefore, we will perform intradermal injection of IgG-isotype or anti-G-CSF antibody into the IMQ-induced psoriatic mice.

Another concern is insufficient demonstration of G-CSF-mediated emergency granulopoiesis in the psoriasis model. All data in Figure 5 were obtained from experiments with only n=3, and adding more replicates, in particular to those in Figure 5B, which show quite some variation in MPP numbers, is recommended. The relatively small reduction of BM granulocyte numbers (Figure 5C) compared to greater depletion of circulating granulocytes (Figure S5A) raises the possibility that it is the mobilization effect rather than granulopoiesis-stimulating effect that skin-derived G-CSF exerts to promote supply of circulating neutrophils that eventually infiltrate into the affected skin. This could also explain the negligible effect of IL-1blockade (Figure S4), which selectively shut off myelopoiesis-stimulating effect of IL-1 (Pietras et al. Nat Cell Biol 2016, PMID: 27111842). Are the HSPCs in the psoriasis model more cycling? Do they show myeloid-skewed differentiation when cultured ex vivo or upon transplantation?

Author's response: Thank you for these critical comments. We agree to do the following experiments to address them:

1) HSPCs quantification in Figure 5 especially the MPPs will be added with more replicates.

2) We will assess cycling status of HSPCs by flow cytometric analysis of Ki67and Propidium Iodide to characterize G0, G1 and G2/M cell cycle phase.

3) To test myeloid-skewed differentiation, Lin- c-Kit+ Sca-1+ cells containing HSPCs will be isolated from bone marrow of Vas/IMQ-treated mice and transplanted into lethally irradiated syngeneic mice.

The authors' claim that skin-derived G-CSF "induces" neutrophil infiltration warrants further clarification. Alternative explanation is that the upregulated neutrophil-attracting chemokines (Figure S1D) could induce infiltration, whereas G-CSF increase the number of neutrophils to circulate in the vessels near the psoriatic skin. This notion seems supported elsewhere (Moos et al. J Invest Dermatol. 2019, PMID: 30684554). Can the infiltration be inhibited by systemically injecting neutralizing antibody of their receptor, CXCR2?

Author's response: The manuscript focuses on the skin-derived G-CSF function as a long-distance signal for emergency granulopoiesis in the bone marrow upon psoriasis, not the chemoattractant property of it. The sentence of interest is "We found that upon psoriasis induction, skin-resident endothelial cells are activated to produce G-CSF which activates emergency granulopoiesis in bone marrow and induces cutaneous infiltration and accumulation of neutrophil that are functionally inflammatory." in line 28-30. In agreement with point #2 from Reviewer#2, the fact that neutrophil recruitment factors (CXCL1, CXCL2, and CXCL5) were upregulated in psoriatic skin (Figure S1D), suggesting a CXCL-mediated neutrophil recruitment. The sentence of concern need to be changed to "We found that upon psoriasis induction, skin-resident endothelial cells are activated to produce G-CSF which activates emergency granulopoiesis in bone marrow, leading to cutaneous accumulation of neutrophil that are functionally inflammatory.". This revised sentence has omitted the proposal that G-CSF directly dictates neutrophils mobilization to the skin, which is not the key message of the study. Therefore, we found that the CXCR2 (CXCLs receptor) blockade experiment may be of the benefit of future studies.

It remains unclear how skin-derived G-CSF accumulates pathogenic neutrophils. The authors state "pathogenic granulopoiesis," but are the circulating neutrophils in the psoriatic mice already "pathogenic" or do they acquire pathogenic phenotype after cutaneous infiltration? Additional RNA-seq to compare circulating and infiltrated neutrophils would answer this question.

Author's response: We appreciate this valuable comment. We will perform RNA-seq with the peripheral blood-circulating neutrophils (CD45+ CD11b+ Ly6G+ Ly6Cmid) versus skin-infiltrating neutrophils from both Vas/IMQ mice.

In addition, how the accumulated pathogenic neutrophils exacerbate the psoriatic changes remains obscure. Although the authors have attempted to correlate Il17a gene expression in infiltrated neutrophils with psoriatic skin changes, the data do not address to what degree it contributes to cutaneous IL-17A protein levels. The data that cutaneous neutrophil depletion leads to subtle decrease in skin IL-17A expression (Figure 2H) rather supports alternative possibilities. For instance, as indicated elsewhere, IL-17A cutaneous tone could be enhanced by neutrophil-mediated augmentation of Th17 or gamma/delta T cell function (Lambert et al. J Invest Dermatol. 2019, PMID: 30528823). Does neutrophil depletion or G-CSF neutralization alter cell numbers or function of cutaneous Th17 and gamma/delta T cells?

Author's response: Thank you for this insightful comment. To better understand the relative contribution of neutrophils to the cutaneous IL-17A tone in the psoriatic skin, we will perform flowcytometric analysis of Th17 and gamma/delta T cells which are widely known as the major source of IL-17 in psoriatic skin of IMQ-induced mice following injection of isotype-matched or anti-Ly6G antibody.

Finally, as the above conclusions rely solely on the IMQ-induced acute psoriasis model, it would be informative if they could be derived from another psoriasis model. IMQ is known to induce unintended systemic inflammation due to grooming-associated ingestion (Gangwar et al. J Invest Dermatol. 2022, PMID: 34953514), and "pathological crosstalk between skin and BM in psoriatic inflammation" could be strengthened by an intradermal injection model.

Author's response: We appreciate the reviewer for bringing this important point. Regarding the systemic inflammation upon psoriasis, the above-cited study reported increased IFN-B expression in the intestines of IMQ-ingested animal (Grine L et al. Sci Rep. 2016, PMID: 26818707 in Gangwar et al. J Invest Dermatol. 2022, PMID: 34953514). We examined several pro-inflammatory cytokines including IFN-b, IFN-g, and IL-6 and in contrast, found no systemic increase in all these cytokines, except for IFN-g downregulation (Explanation Figure 1), which suggests no evidence of grooming-associated ingestion.

We also examined the Csf3 expression across several distinctively located tissues which showed a selective upregulation in the skin (Figure 4C), suggesting a skin-restricted perturbation. In addition, one study showed that IMQ-ingestion didn't alter number of gut injury-associated CXCR3+ macrophages nor did it aggravate skin inflammation (Pinget et al. Cell Reports. 2022, PMID: 35977500). Together, these findings support that IMQ-induced psoriasis by topical cutaneous application used in our study elicit a local inflammation but not systemic inflammation.

The authors, however, realize that testing alternative psoriasis model such as intradermal injection of IL-23 (Chan et al. J Exp Med. 2006, PMID: 17074928) will strengthen the skin-local insults within the psoriasis model employed, and should be tested in the future.

Minor comments

Figure 1E shows multiple elongated Ly6G+ structures in d0-2 control and d0 IMQ skins that do not appear to be neutrophils.

Author's response: We appreciate the Reviewer#1 pointing this issue. As mentioned by the Reviewer#1, the elongated structures detected in the intravital microscopy are not neutrophils, but autofluorescence from the skin bulge regions (Wun et al. J Invest Dermatol. 2005, PMID: 15816847). We have eliminated these unspecific signals from the transformation and quantification (Figure 1F, S1G, and S1H). We will also add an explanatory sentence in Materials and Methods section "Of note, the fluorescent signal with elongated structures resembling hair bulge were autofluorescence and thus removed from further analysis." to be more precise about our methods.

In Figure 2C, the bottom GSEA seems to be showing type II IFN response, not type I IFN, according to the text.

Author's response: Thank you for the comment, we will correct this misspelling.

Author's response: We appreciate that Reviewer#1 bring up this point. We examined the kinetics of the bone marrow cellularity and GMPs across 4 days of psoriasis induction in mice. The bone marrow cell number was lowered along that span with lowermost count at 2 days. Consistent to the BM-cellularity, the GMP number was also lowered about one-third in the first 2 days of psoriasis. This kinetic is consistent with the previous report showing a rapid reduction of GMPs in the bone marrow within 2 days following systemic G-CSF administration driven emergency granulopoiesis (Hirai et al. Nat. Immunol. 2006, PMID: 16751774). From 2 days to 4 days, the GMP number rapidly increased to slightly above basal number (Explanation Figure 2). This timely coordinated expansion suggests a significant supply of GMPs from the differentiating upstream myeloid progenitors (Figure 3B).

When the psoriatic mice with elevated G-CSF is injected with anti-G-CSF or IgG-isotype antibody, the bone marrow cellularity and GMP numbers at 4 days were (Explanation Figure 3). Firstly, as psoriasis reduced bone marrow cellularity (Explanation Figure 2), the unchanged number after anti-G-CSF injection indicates that administration of 10µg/day for 4 days does not significantly affect mobilization of psoriatic bone marrow cells. Secondly, the similar GMP numbers at 4 days psoriasis is plausibly due to snapshot analysis when it has already in the numerical recovery period (Explanation Figure 2). Importantly, the notion that anti-G-CSF injection to psoriatic mice reduced granulocytes in the bone marrow, peripheral blood, and skin suggesting G-CSF as a key mediator in psoriatic driven emergency granulopoiesis on top of unlikely case of ineffective anti-G-CSF treatment.

Taken together, these data suggest a G-CSF mediated emergency granulopoiesis occurrence in the IMQ-induced psoriasis. We will put these data into a revised Figure.

In Figures 6B, in which cluster of human skin cells IL-17A expression would be enriched?

Author's response: Thank you for this important point. The IL-17A expression is found in the T-cell cluster (Explanation Figure 4). We also expected to see IL-17A contribution from other cell subset(s), in particular neutrophil. However, due to the fragile nature of neutrophils and thereby, technical difficulty to get their sequencing reads, this dataset (GSE173706) doesn't contain neutrophils, but rather monocytes, macrophages, and dendritic cells among the myeloid subset (Explanation Figure 5). With this, it leaves open the question on what potential contribution of IL-17A produced by neutrophils is in human psoriasis (Reich et al. Exp. Dermatol. 2015, PMID: 25828362).

Figure 1E shows multiple elongated Ly6G+ structures in d0-2 control and d0 IMQ skins that do not appear to be neutrophils.

Author's response: We appreciate the Reviewer#1 pointing this issue. As mentioned by the Reviewer#1, the elongated structures detected in the intravital microscopy are not neutrophils, but autofluorescence from the skin bulge regions (Wun et al. J Invest Dermatol. 2005, PMID: 15816847). We have eliminated these unspecific signals from the transformation and quantification (Figure 1F, S1G, and S1H). We will also add an explanatory sentence in Materials and Methods section "Of note, the fluorescent signal with elongated structures resembling hair bulge were autofluorescence and thus removed from further analysis." to be more precise about our methods.

In Figure 2C, the bottom GSEA seems to be showing type II IFN response, not type I IFN, according to the text.

Author's response: Thank you for the comment, we will correct this misspelling.

Reviewer#2

1. Interpretation of neutrophil transcriptomic changes (Figure 2)

The RNA-seq analysis reveals substantial downregulation of several canonical pro inflammatory pathways in neutrophils from psoriatic skin, including IL-6, IL-1, and type II interferon signaling. The authors should discuss the functional relevance of this unexpected transcriptional repression. For example, does this indicate a shift toward specialized effector functions rather than classical cytokine responsiveness? More importantly, the most striking transcriptional change is the upregulation of NADPH oxidase-related genes (e.g., Nox1, Nox3, Nox4, Enox2). This suggests an oxidative stress-driven pathogenic mechanism, potentially more relevant than IL-17A production. Yet this aspect is not explored in the manuscript. Assessing ROS levels or oxidative neutrophil effector functions in this model would considerably strengthen the mechanistic link. Conversely, although IL-17A is upregulated in neutrophils, neutrophil depletion reduces total Il17a expression in skin only partially. This indicates that neutrophils are unlikely to be the dominant IL-17A source in the lesion. The authors' focus on neutrophil-derived IL 17A therefore seems overstated. A more rigorous assessment-e.g., conditional deletion of Il17a specifically in neutrophils-would be required to establish its true contribution. Taken together, the data suggest that oxidative programs, rather than IL-17A production, may represent the principal pathogenic axis downstream of neutrophils, and this deserves deeper discussion.

Author's response: Thank you for raising this valuable views. We have agreed to address these critical points by the following approaches:

1) To address the changes in NADPH oxidase-related gene signature, we will measure ROS production in the neutrophils from skin and peripheral blood with DHR123.

2) Responding to the IL17A contribution by neutrophils, we will flow cytometrically assess the Th17 and gamma/delta T cell population in the skin of psoriatic mice treated with anti-Ly6G or isotype-matched antibody as was suggested by Reviewer#1.

3) We will discuss downregulation of the canonical pro inflammatory and IL-17 pathways in the psoriatic neutrophils in the discussion.

Human data reanalysis (Figure 6):

The re-analysis of bulk and single-cell RNA-seq datasets is valuable but incomplete. Several mechanistically relevant questions could be addressed with the available data:

2.1. GM-CSF (CSF2) is also strongly upregulated in psoriatic lesions (bulk RNA-seq). It would be informative to determine whether endothelial cells also express CSF2 in the scRNA-seq dataset, as this would suggest coordinated regulation of myeloid-supporting cytokines.

2.2. Myeloid cell subsets should be examined more closely. A comparison of human myeloid transcriptomes with the mouse neutrophil RNA-seq would clarify whether similar IL-17A-related or NADPH oxidase-related signatures occur in human disease. In particular, which cell types express IL17A in human lesions?

2.3. Chemokine production should be attributed to specific cell types. Bulk RNA-seq confirms strong induction of CXCL1, CXCL2, CXCL5, but the scRNA-seq dataset allows determining whether these chemokines originate from endothelial cells or other stromal/immune populations. This information is important for defining whether endothelial cells coordinate both neutrophil recruitment and granulopoiesis.

Addressing these points would make the human-mouse comparison substantially stronger.

Author's response: Thank you for pointing these important issues. By reanalyzing the dataset, we found several points regarding the comments, as follows:

2.1) CSF2 is expressed by T-cell cluster in the human skin dataset (Explanation Figure 4), in agreement with previous murine study (Hartwig et al. Cell Reports. 2018, PMID: 30590032). We will add this data in the revised manuscript.

2.2) In line with point#10 from Reviewer#1, the dataset clearly shows T-cell cluster as the main IL17A source (Explanation Figure 4 above). The dataset, however, doesn't contain phenotypic neutrophils (CEACAM (CD66b) and PGLYRP1) but monocytes, macrophages, and dendritic cells (Explanation Figure 5 above). This loss was probably due to a technical limitation given the difficulty in capturing sequencing reads from fragile neutrophils. Therefore, it is no longer possible to reanalyze IL-17 expression in the absence of neutrophils in the datapool.

2.3) Reanalysis of CXCLs in the human scRNAseq dataset (GSE173706) clarified their secretion dynamics and cellular sources under normal and psoriatic condition. In normal skin, all examined cell subsets show only low CXCLs expression. In contrast, psoriatic skin exhibits significant CXCLs upregulation with distinct cell subsets clearly showing dramatic upregulation, potentially being the major CXCLs source. CXCL1 is markedly upregulated in fibroblasts, myeloid cells, and melanocyte and nerve cells. CXCL2 is strikingly upregulated to myeloid cells, while CXCL5 is hugely increased in fibroblasts, myeloid cells, and mast cells (Explanation Figure 7). Taken together, these results suggest that CXCLs upregulation in the psoriatic skin is coordinatively executed by both stromal and immune compartments. Of note, the endothelial cells show minimal changes in CXCLs expression, even downregulate CXCL2 in psoriasis, indicating that they are unlikely to be the major contributor to CXCL-mediated neutrophil recruitment.

**Referees cross-commenting**

I agree with Reviewer 1 that the contribution of EC-derived G-CSF to circulating G-CSF levels and to emergency myelopoiesis requires additional genetic or neutralization experiments to be fully established.

Author's response: We appreciate that Reviewer#2 raised this key point. In addition to examining the serum G-CSF upon intradermal anti-G-CSF administration in point#1 from Reviewer#1 above, we will also examine the emergency myelopoiesis signs in vivo.

Minor points

1. Line 319: the text likely refers to Figure S4, not S3.

Author's response: Thank you, we will correct the nomenclature.

Line 338: "psoriatic" is misspelled.

Author's response: Thank you, we will change this to "psoriatic".

Reviewer #3

• Place the work in the context of the existing literature (provide references, where appropriate).

Psoriasis is extensively studied, a good recent reference- https://doi.org/10.1016/j.mam.2024.101306

Author's response: Thank you for Reviewer#3's suggestion. The referenced study highlights the current paradigm that largely focus on skin-restricted mechanism and overlook potential cross-organ interaction in the psoriasis inflammation. Our findings provide a new insight into the skin-bone marrow crosstalk in the disease context. In addition, the suggested reference underscores the key roles of diverse innate immune cells including neutrophils, eosinophils, dendritic cells, etc. which is fundamental for our study and might also guide future exploration of additional innate cell subsets beyond neutrophils. We will therefore include the mentioned reference to our revised manuscript.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

It is all good. May add graphical-abstract.

Author's response: Thank you for the reviewer's input, we agree that a graphical-abstract will help the readers more clearly grasp the key messages of our manuscript. We will include it in the revised manuscript.

Major comments:

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

No. It is very solid.

Author's response: We appreciate the reviewer's view that the claims in our paper are solid.

• 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.

Such a discovery clearly opens many options, and it is fascinating to suggest additional experiments for future studies. It is a complete study, best to publish as-is and let many to read and proceed with this new concept.

Author's response: We thank the reviewer for noting that the current experimental evidence is complete that no additional experiments are necessary at this stage. We agree that the discovery opens prospective directions for future studies.

• 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.

N/A - I suggest no additional experiments at this point. Get it published and see how many will follow this new direction!

Author's response: We thank the reviewer for recognizing that the experimental data has been sufficient to be a foundation for the future research.

• Are the data and the methods presented in such a way that they can be reproduced?

Yes.

Author's response: We thank the reviewer for recognizing that our methods are reproducible.

• Are the experiments adequately replicated, and is the statistical analysis adequate?

Yes. The data are of very high quality.

Author's response: We are grateful that the reviewer view our replication strategy and statistical analysis are of a high quality.

Minor comments:

• Specific experimental issues that are easily addressable.

None. It is good as-is. One may always suggest minor things- but this one is better published so many laboratories may rush for this new direction. I think it will be interesting studying some long-term impacts, and changes not only of neutrophils but also of other innate cells, such as DCs, Macrophages, and Eosinophils - so it is best to let laboratories that focus on these cells know of the discovery and pursue independent studies.

Author's response: We appreciate the reviewer's assessment that our paper is already well set for the community to explore the newly proposed direction.

• Are the text and figures clear and accurate?

Yes.

Author's response: We thank the reviewer's evaluation. We have ensured that the text and figures in our manuscript are clear and accurate. Once again, we thank the reviewer for the encouraging and constructive appraisal. We are pleased that the reviewer find the manuscript has already been strong and suitable for publication.

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

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Reply to the reviewers

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

Summary The manuscript by Aarts et al. explores the role of GRHL2 as a regulator of the progesterone receptor (PR) in breast cancer cells. The authors show that GRHL2 and PR interact in a hormone-independent manner and based on genomic analyses, propose that they co-regulate target genes via chromatin looping. To support this model, the study integrates both newly generated and previously published datasets, including ChIP-seq, CUT&RUN, RNA-seq, and chromatin interaction assays, in breast cancer cell models (T47DS and T47D).

Major comments: R1.1 Novelty of GRHL2 in steroid receptor biology The role of GRHL2 as a co-regulator of steroid hormone receptors has previously been described for ER (J Endocr Soc. 2021;5(Suppl 1):A819) and AR (Cancer Res. 2017;77:3417-3430). In the ER study, the authors also employed a GRHL2 ΔTAD T47D cell model. Therefore, while this manuscript extends GRHL2 involvement to PR, the contribution appears incremental rather than conceptual.

We are fully aware of the previously described role of GRHL2 as a co-regulator of steroid hormone receptors, particularly ER and AR. As acknowledged in our introduction (lines 104-108), we explicitly state: "Grainyhead-like 2 (GRHL2) has recently emerged as a potential pioneer factor in hormone receptor-positive cancers, including breast cancer21. However, nearly all studies to date have focused on GRHL2 in the context of ER and estrogen signaling, leaving its role in PR- and progesterone-mediated regulation unexplored22-26".

As for the specific publications that the reviewer refers to: The first refers to an abstract from an annual meeting of the Endocrine Society. As we have been unable to assess the original data underpinning the abstract - including the mentioned GRHL2 DTAD model - we prefer not to cite this particular reference. We do cite other work by the same authors (Reese et al. 2022, our ref. 25). We also cite the AR study mentioned by the reviewer (our ref. 55) in our discussion. As such, we think we do give credit to prior work done in this area.

By characterizing GRHL2 as a co-regulator of the progesterone receptor (PR), we expand on the current understanding of GRHL2 as a common transcriptional regulator within the broader context of steroid hormone receptor biology. Given that ER and PR are frequently co-expressed and active within the same breast cancer cells, our findings raise the important possibility that GRHL2 may actively coordinate or modulate the balance between ER- and PR-driven transcriptional programs, as postulated in the discussion paragraph.

Importantly, we also functionally link PR/GRHL2-bound enhancers to their target genes (Fig5), providing novel insights into the downstream regulatory networks influenced by this interaction. These results not only offer a deeper mechanistic understanding of PR signaling in breast cancer but also lay the groundwork for future comparative analyses between GRHL2's role in ER-, AR-, and PR-mediated gene regulation.

As such, we respectfully suggest that our work offers more than an incremental advance in our knowledge and understanding of GRHL2 and steroid hormone receptor biology.

R1.2 Mechanistic depth The study provides limited mechanistic insight into how GRHL2 functions as a PR co-regulator. Key mechanistic questions remain unaddressed, such as whether GRHL2 modulates PR activation, the sequential recruitment of co-activators/co-repressors, engages chromatin remodelers, or alters PR DNA-binding dynamics. Incorporating these analyses would considerably strengthen the mechanistic conclusions.

Although our RNA-seq data demonstrate that GRHL2 modulates the expression of PR target genes, and our CUT&RUN experiments show that GRHL2 chromatin binding is reshaped upon R5020 exposure, we acknowledge that we have not further dissected the molecular mechanisms by which GRHL2 functions as a PR co-regulator.

We did consider several follow-up experiments to address this, including PR CUT&RUN in GRHL2 knockdown cells, CUT&RUN for known co-activators such as KMT2C/D and P300, as well as functional studies involving GRHL2 TAD and DBD mutants. However, due to technical and logistical challenges, we were unable to carry out these experiments within the timeframe of this study.

That said, we fully recognize that such approaches would provide deeper mechanistic insight into the interplay between PR and GRHL2. We have therefore explicitly acknowledged this limitation in our limitations of the study section (line 502-507) and mention this as an important avenue for future investigation.

R1.3 Definition of GRHL2-PR regulatory regions (Figure 2) The 6,335 loci defined as GRHL2-PR co-regulatory regions are derived from a PR ChIP-seq performed in the presence of hormone and a GRHL2 ChIP-seq performed in its absence. This approach raises doubts about whether GRHL2 and PR actually co-occupy these regions under ligand stimulation. GRHL2 ChIP-seq experiments in both hormone-treated and untreated conditions are necessary to provide stronger support for this conclusion.

Although bulk ChIP-seq cannot definitively demonstrate simultaneous binding of PR and GRHL2 at the same genomic regions, we agree that the ChIP-seq experiments we present do not provide a definitive answer on if GRHL2 and PR co-occupy these regions under ligand stimulation. As a first step to address this, we performed CUT&RUN experiments for both GRHL2 and PR under untreated and R5020-treated conditions. These experiments revealed a subset of overlapping PR and GRHL2 binding sites (approximately {plus minus}5% of the identified PR peaks under ligand stimulation).

We specifically chose CUT&RUN to minimize artifacts from crosslinking and sonication, thereby reducing background and enabling the mapping of high-confidence direct DNA-binding events: Given that a fraction of GRHL2 physically interacts with PR (Fig1D), it is possible that ChIP-seq detects indirect binding of GRHL2 at PR-bound sites and vice versa. CUT&RUN, by contrast, allows us to identify direct binding sites with higher confidence.

Nonetheless, although outside the scope of the current manuscript, we agree that a dedicated GRHL2 ChIP with and without ligand stimulation would provide additional insight, and we have accordingly added this suggestion to the discussion (line 502-507).

R1.4 Cell model considerations The manuscript relies heavily on the T47DS subclone, which expresses markedly higher PR levels than parental T47D cells (Aarts et al., J Mammary Gland Biol Neoplasia 2023; Kalkhoven et al., Int J Cancer 1995). This raises concerns about physiological relevance. Key findings, including co-IP and qPCR-ChIP experiments, should be validated in additional breast cancer models such as parental T47D, BT474, and MCF-7 cells to generalize the conclusions. Furthermore, data obtained from T47D (PR ChIP-seq, HiChIP, CTCF and Rad21 ChIP-seq) and T47DS (RNA-seq, CUT&RUN) are combined along the manuscript. Given the substantial differences in PR expression between these cell lines, this approach is problematic and should be reconsidered.

We agree that physiological relevance is important to consider. Here, all existing model systems have some limitations. In our experience, it is technically challenging to robustly measure gene expression changes in parental T47D cells (or MCF7 cells, for that matter) in response to progesterone stimulation (Aarts et al., J Mammary Gland Biol Neoplasia 2023). As we set out to integrate PR and GRHL2 binding to downstream target gene induction, we therefore opted for the most progesterone responsive model system (T47DS cells). We agree that observations made in T47D and T47DS cells should not be overinterpreted and require further validation. We have now explicitly acknowledged this and added it to the discussion (line 507-509).

As for the reviewer's suggestion to use MCF7 cells: apart from its suboptimal PR-responsiveness, this cell line is also known to harbor GRHL2 amplification, resulting in elevated GRHL2 levels (Reese et al., Endocrinology2019). By that line of reasoning, the use of MCF7 cells would also introduce concerns about physiological relevance. That being said, and as noted in the discussion (line 390-391), the study by Mohammed et al. which identified GRHL2 as a PR interactor using RIME, was performed in both MCF7 and T47D cells. This further supports the notion that the PR-GRHL2 interaction is not limited to a single cell line.

R1.5 CUT&RUN vs ChIP-seq data The CUT&RUN experiments identify fewer than 10% of the PR binding sites reported in the ChIP-seq datasets. This discrepancy likely results from methodological differences (e.g., absence of crosslinking, potential loss of weaker binding events). The overlap of only 158 sites between PR and GRHL2 under hormone treatment (Figure 3B) provides limited support for the proposed model and should be interpreted with greater caution.

We acknowledge the discrepancy between the number of binding sites between ChIP-seq and CUT&RUN. Indeed, methodological differences likely contribute to the differences in PR binding sites reported between the ChIP-seq and CUT&RUN datasets. As the reviewer correctly notes, the absence of crosslinking and sonication in CUT&RUN reduces detection of weaker binding events. However, it also reduces the detection of indirect binding events which could increase the reported number of peaks in ChIPseq data (e.g. the common presence of "shadow peaks").

As also discussed in our response to R1.3, we deliberately chose the CUT&RUN approach to enable the identification of high-confidence direct DNA-binding events. Since GRHL2 physically interacts with PR, ChIP-seq could potentially capture indirect binding of GRHL2 at PR-bound sites, and vice versa. By contrast, CUT&RUN primarily captures direct DNA-protein interactions, offering a more specific binding profile. Thus, while the number of CUT&RUN binding sites is much smaller than previously reported by ChIP-seq, we are confident that they represent true, direct binding events.

We would also like to emphasize that the model presented in figure 6 does not represent a generic or random gene, but rather a specific gene that is co-regulated by both GRHL2 and PR. In this specific case, regulation is proposed to occur via looping interactions from either individual TF-bound sites (e.g., PR-only or GRHL2-only) or shared GRHL2/PR sites. We do not propose that only shared sites are functionally relevant, nor do we assume that GRHL2 and PR must both be directly bound to DNA at these shared sites. Therefore, overlapping sites identified by ChIP-seq-potentially reflecting indirect binding events-could indeed be missed by CUT&RUN, yet still contribute to gene regulation. To clarify this, we have revised the main text (line 331-334) and the legend of Figure 6 to explicitly state that the model refers to a gene with established co-regulation by both GRHL2 and PR.

R1.6 Gene expression analyses (Figure 4) The RNA-seq analysis after 24 hours of hormone treatment likely captures indirect or secondary effects rather than the direct PR-GRHL2 regulatory program. Including earlier time points (e.g., 4-hour induction) in the analysis would better capture primary transcriptional responses. The criteria used to define PR-GRHL2 co-regulated genes are not convincing and may not reflect the regulatory interactions proposed in the model. Strong basal expression changes in GRHL2-depleted cells suggest that much of the transcriptional response is PR-independent, conflicting with the model (Figure 6). A more straightforward approach would be to define hormone-regulated genes in shControl cells and then examine their response in GRHL2-depleted cells. Finally, integrating chromatin accessibility and histone modification datasets (e.g., ATAC-seq, H3K27ac ChIP-seq) would help establish whether PR-GRHL2-bound regions correspond to active enhancers, providing stronger functional support for the proposed regulatory model.

We thank the reviewer for pointing this out. We now recognize that our criteria for selecting PR/GRHL2 co-regulated genes were not clearly described. To address this, we have revised our approach as per the reviewer's suggestion: we first identified early and sustained PR target genes based on their response at 4 and 24 hours of induction and subsequently overlaid this list with the gene expression changes observed in GRHL2-depleted cells. This revised approach reduced the amount of PR-responsive, GRHL2 regulated target genes from 549 to 298 (46% reduction). We consequently updated all following analyses, resulting in revised figures 4 and 5 and supplementary figures 2,3 and 4. As a result of this revised approach, the number of genes that are transcriptionally regulated by GRHL2 and PR (RNAseq data) that also harbor a PR loop anchor at or near their TSS after 30 minutes of progesterone stimulation (PR HiChIP data) dropped from 114 to 79 (30% reduction). We thank the reviewer for suggesting this more straightforward approach and want to emphasize that our overall conclusions remain unaltered.

As above in our response to R1.3, we want to emphasize that the model presented in figure 6 does not depict a generic or randomly chosen gene, but a gene that is specifically co-regulated by both GRHL2 and PR. We also want to emphasize that the majority of GRHL2's transcriptional activity is PR-independent. This is consistent with the limited fraction of GRHL2 that co-immunoprecipitated with PR (Figure 1D), and with the well-established roles of GRHL2 beyond steroid receptor signaling. In fact, the overall importance of GRHL2 for cell viability in T47D(S) cells is underscored by our inability to generate a full knockout (multiple failed attempts of CRISPR/Cas mediated GRHL2 deletion in T47D(S) and MCF7 cells), and by the strong selection we observed against high-level GRHL2 knockdown using shRNA.

As for the reviewer's suggestion to assess whether GRHL2/PR co-bound regions correspond to active enhancers by integrating H3K27ac and ATAC-seq data: We have re-analyzed publicly available H3K27ac and ATAC-seq datasets from T47D cells (references 42 and 43). These analyses are now added to figure 2 (F and G). The H3K27Ac profile suggests that GRHL2-PR overlapping sites indeed correspond to more active enhancers (Figure 2F), with a proposed role for GRHL2 since siGRHL2 affects the accessibility of these sites (Figure 2G).

Minor comments Page 19: The statement that "PR and GRHL2 trigger extensive chromatin reorganization" is not experimentally supported. ATAC-seq would be an appropriate method to test this directly.

We agree with the reviewer and have removed this sentence, as it does not contribute meaningfully to the flow of the manuscript.

Prior literature on GRHL2 as a steroid receptor co-regulator should be discussed more thoroughly.

We now added additional literature on GRHL2 as a steroid hormone receptor co-regulator in the discussion (line 397-401) and we cite the papers suggested by R1 in R1.1 (references 25 and 54).

Reviewer #1 (Significance (Required)):

The identification of novel PR co-regulators is an important objective, as the mechanistic basis of PR signaling in breast cancer remains incompletely understood. The main strength of this study lies in highlighting GRHL2 as a factor influencing PR genomic binding and transcriptional regulation, thereby expanding the repertoire of regulators implicated in PR biology.

That said, the novelty is limited, given the established roles of GRHL2 in ER and AR regulation. Mechanistic insight is underdeveloped, and the reliance on an engineered T47DS model with supra-physiological PR levels reduces the general impact. Without validation in physiologically relevant breast cancer models and clearer separation of direct versus indirect effects, the overall advance remains modest.

The manuscript will be of interest to a specialized audience in the fields of nuclear receptor signaling, breast cancer genomics, and transcriptional regulation. Broader appeal, including translational or clinical relevance, is limited in its current form.

We have addressed all of these points in our response above and agree that with our implemented changes, this study should reach (and appeal to) an audience interested in transcriptional regulation, chromatin biology, hormone receptor signaling and breast cancer.

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

The authors present a study investigating the role of GRHL2 in hormone receptor signaling. Previous research has primarily focused on GRHL2 interaction with estrogen receptor (ER) and androgen receptor (AR). In breast cancer, GRHL2 has been extensively studied in relation to ER, while its potential involvement with the progesterone receptor (PR) remains largely unexplored. This is the rationale of this study to investigate the relation between PR and GRHL2. The authors demonstrate an interaction between GRHL2 and PR and further explore this relationship at the level of genomic binding sites. They also perform GRHL2 knockdown experiments to identify target genes and link these transcriptional changes back to GRHL2-PR chromatin occupancy. However, several conceptual and technical aspects of the study require clarification to fully support the authors' conclusions.

R2.1 Given the high sequence similarity among GRHL family members, this raises questions about the specificity of the antibody used for GRHL2 RIME. The authors should address whether the antibody cross-reacts with GRHL1 or GRHL3. For example, GRHL1 shows a higher log fold change than GRHL2 in the RIME data.

Indeed, GRHL1, GRHL2, and GRHL3 are structurally related. They share a similar domain organization and are all {plus minus}70kDa in size. Sequence similarity is primarily confined to the DNA-binding domain, with GRHL2 and GRHL3 showing 81% similarity in this region, and GRHL1 showing 63% similarity to GRHL2/3 (Ming, Nucleic Acids Res 2018).

The antibody used, sourced from the Human Protein Atlas, is widely used in the field. It targets an epitope within the transactivation domain (TAD) of GRHL2-a region with relatively low sequence similarity to the corresponding domains in GRHL1 and GRHL3.

We assessed the specificity of the antibody using western blotting (Supplementary Figure 2A) in T47DS wild-type and GRHL2 knockdown cells. As expected, GRHL2 protein levels were reduced in the knockdown cells providing convincing evidence that the antibody recognizes GRHL2. The remaining signal in shGRHL2 knockdown cells could either be due to remaining GRHL2 protein or due to the antibody detecting GRHL1/3. Furthermore, the observed high log-fold enrichment of GRHL1 in our RIME may reflect known heterodimer formation between GRHL1 and GRHL2, rather dan antibody cross-reactivity. As such, we cannot formally rule out cross-reactivity and have mentioned this in the limitations section (line 497-501).

R2.2 In addition, in RIME experiments, one would typically expect the bait protein to be among the most highly enriched proteins compared to control samples. If this is not the case, it raises questions about the efficiency of the pulldown, antibody specificity, or potential technical issues. The authors should comment on the enrichment level of the bait protein in their data to reassure readers about the quality of the experiment.

We agree with the reviewer that this information is crucial for assessing the quality of the experiment. We have therefore added the enrichment levels (log₂ fold change of IgG control over pulldown) to the methods section (line 592).

As the reviewer notes, GRHL2 was not among the top enriched proteins in our dataset. This is due to unexpectedly high background binding of GRHL2 to the IgG control antibody/beads, for which we currently have no explanation. As a result, although we detected many unique GRHL2 peptides, observed high sequence coverage (>70%), and GRHL2 ranked among the highest in both iBAQ and LFQ values, its relative enrichment was reduced due to the elevated background. During our RIME optimization, Coomassie blue staining of input and IP samples revealed a band at the expected molecular weight of GRHL2 in the pull down samples that was absent in the IgG control (see figure 1 for the reviewer below, 4 right lanes), supporting the conclusion that GRHL2 is specifically enriched in our GRHL2 RIME samples. Combined with enrichment of some of the expected interacting proteins (e.g. KMT2C and KMT2D), we are convinced that the experiment of sufficient quality to support our conclusions.

Figure 1 for reviewer: Coomassie blue staining of input and IP GRHL2 and IgG RIME samples. NT = non-treated, T = treated.

R2.3 The authors report log2 fold changes calculated using iBAQ values for the bait versus IgG control pulldown. While iBAQ provides an estimate of protein abundance within samples, it is not specifically designed for quantitative comparison between samples without appropriate normalization. It would be helpful to clarify the normalization strategy applied and consider using LFQ intensities.

We understand the reviewer's concern. Due to the high background observed in the IgG control sample (see R2.2), the LFQ-based normalization did not accurately reflect the enrichment of GRHL2, which was clearly supported by other parameters such as the number of unique peptides (see rebuttal Table 1). After discussions with our Mass Spectrometry facility, we decided to consider the iBAQ values-which reflect the absolute protein abundance within each sample-as a valid and informative measure of enrichment. In the context of elevated background levels, iBAQ provides an alternative and reliable metric for assessing protein enrichment and was therefore used for our interactor analysis.

Unique peptides

IBAQ GRHL2

IBAQ IgG

LFQ GRHL2

LFQ IgG

GRHL2

52

1753400.00

155355.67

5948666.67

3085700.00

GRHL1

23

56988.33

199.03

334373.33

847.23

*Table 1. Unique peptide, IBAQ and LFQ values of the GRHL2 and IgG pulldowns for GRHL2 and GRHL1 *

R2.4 Other studies have reported PR RIME, which could be a valuable source to investigate whether GRHL proteins were detected.

We thank the reviewer for pointing this out. We are aware of the PR RIME, generated by Mohammed et al., which we refer to in the discussion (lines 390-391). This study indeed identified GRHL2 as a PR-interacting protein in MCF7 and T47D cells. Although they do not mention this interaction in the text, the interaction is clearly indicated in one of the figures from their paper, which supports our findings. To our knowledge, no other PR RIME datasets in MCF7 or T47D cells have been published to date.

R2.5 In line 137, the term "protein score" is mentioned. Could the authors please clarify what this means and how it was calculated.

We agree that this point was not clearly explained in the original text. The scores presented reflect the MaxQuant protein identification confidence, specifically the sum of peptide-level scores (from Andromeda), which indicates the relative confidence in protein detection. We have now added this clarification to line 137 and to the legend of Figure 1.

R2.6 In line 140-141. The fact that GRHL2 interacts with chromatin remodelers does not by itself prove that GRHL2 acts as a pioneer factor or chromatin modulator. Demonstrating pioneer function typically requires direct evidence of chromatin opening or binding to closed chromatin regions (e.g., ATAC-seq, nucleosome occupancy assays). I recommend revising this statement or providing supporting evidence.

We agree that the fact that GRHL2 interacts with chromatin remodelers does not by itself prove that GRHL2 acts as a pioneer factor or chromatin modulator. However, a previous study (Jacobs et al, Nature genetics, 2018) has shown directly that the GRHL family members (including GRHL2) have pioneering function and regulate the accessibility of enhancers. We adapted line 140-141 to state this more clearly. In addition, our newly added data in Figure 2G also support the fact that GRHL2 has a role in regulating chromatin accessibility in T47D cells.

R2.7 The pulldown Western blot lacks an IgG control in panel D.

This is correct. As the co-IP in Figure 1D served as a validation of the RIME and was specifically aimed at determining the effect of hormone treatment on the observed PR/GRHL2 interaction, we did not perform this control given the scale of the experiment. However, during RIME optimization, we performed GRHL2 staining of the IgG controls by western blot, shown in figure 2 for the reviewer below. As stated above, some background GRHL2 signal was observed in the IgG samples, but a clear enrichment is seen in the GRHL2 IP.

Taken together, we believe that the well-controlled RIME, combined with the co-IP presented, provides strong evidence that the observed signal reflects a genuine GRHL-PR interaction.

Figure 2 for reviewer: WB of input and IP GRHL2 and IgG RIME samples stained for GRHL2. NT = non-treated, T = treated

R2.8 Depending on the journal and target audience, it may be helpful to briefly explain what R5020 is at its first mention (line 146).

Thank you. We have adapted this accordingly.

R2.9 The authors state that three technical replicates were performed for each experimental condition. It would be helpful to clarify the expected level of overlap between biological replicates of RIME experiments. This clarification is necessary, especially given the focus on uniquely enriched proteins in untreated versus treated cells, and the observation that some identified proteins in specific conditions are not chromatin-associated. Replicates or validations would strengthen the findings.

We use the term technical rather than biological replicates because for cell lines, defining true biological replicates is challenging, as most variability arises from experimental rather than biological differences. To introduce some variation, we split our T47DS cells into three parallel dishes 5 days prior to starting the treatment. We purposely did this, to minimize to minimize the likelihood that proteins identified as uniquely enriched are artifacts. Each of the three technical replicates comes from one of these three parallel splits (so equal passage numbers but propagated in parallel dishes for 5 days before the start of the experiment).

To generate the three technical replicates for our RIME, we plated cells from the parallel grown splits. Treatments for the three replicates were performed per replicate. Samples were crosslinked, harvested and lysed for subsequent RIME analysis, the three replicates were processed in parallel, for technical and logistical reasons. To clarify the experimental setup, we have updated the methods section accordingly (lines 566-568).

As for the detection of non-chromatin-associated proteins: We cannot rule out that these are artifacts, as they may arise from residual cytosolic lysate during nuclear extraction. Alternatively, they could reflect a more dynamic subcellular localization of these proteins than currently annotated or appreciated.

R2.10 The volcano plot for the RIME experiment appears to show three distinct clusters of proteins on the right, which is unusual for this type of analysis. The presence of these apparent groupings may suggest an artifact from the data processing, such as imputation. Can the authors clarify the origin of these groupings? If it is due to imputation or missing values, I recommend applying a stricter threshold, such as requiring detection in all three replicates (3/3) to improve the robustness of the enrichment analysis and increase confidence in the identified interactors.

We thank the reviewer for pointing this out. As suggested, we re-evaluated the imputation and applied a stricter threshold, requiring detection in all three replicates. Indeed, the separate clusters were due to missing values, therefore we now revised the imputation method by imputing values based on the normal distribution. Using this revised analysis, we identify 2352 GRHL2 interactors instead of 1140, but the number of interacting proteins annotated as transcription factors or chromatin-associated/modifying proteins was still 103. Figure 1B, 1E, and Supplementary Figure 4A have been updated accordingly. We also revised the methods section to reflect this change. We think this suggestion has improved our analysis of the data and we thank the reviewer for pointing this out.

R2.11 The statement that "PR and GRHL2 frequently overlap" may be overstated given that only ~700 overlapping sites are reported (cut&run).

We have replaced "frequently overlap" by "can overlap" (line 229-230).

R2.12 The model in Figure 6 suggests limited chromatin occupancy of PR and GRHL2 in hormone-depleted conditions, consistent with the known requirement of ligand for stable PR-DNA binding. However, Figure 1 shows no major difference in GRHL2-PR interaction between untreated and hormone-treated cells. This raises questions about where and how this interaction occurs in the absence of hormone. Since PR binding to chromatin is typically minimal without ligand, can the authors clarify this given that RIME data reflect chromatin-bound interactions.

Indeed, the model in figure 6 suggests limited chromatin occupancy of PR and GRHL2 under hormone-depleted conditions. It is, however, important to note that the locus shown represents a gene regulated by both PR and GRHL2 - and not just any gene. We recognize that this was not sufficiently clear in the original version, and we have now clarified this in both the main text (line 331-334) and the figure legend.

We propose that PR and GRHL2 bind or become enriched at enhancer sites associated with their target genes upon ligand stimulation. This is consistent with the known requirement of ligand for stable PR-DNA binding and with our observation that PR/GRHL2 overlapping peaks are detected only in the ligand-treated condition of the CUT&RUN experiment. Given the broader role of GRHL2, it also binds chromatin independently of progesterone and the progesterone receptor, which is why we included-but did not focus on-GRHL2-only binding events in our model.

We would also like to clarify that, although RIME includes a nuclear enrichment step that enriches for chromatin-associated proteins, the pulldown is performed on nuclear lysates. Therefore, it captures both chromatin-bound protein complexes and freely soluble nuclear complexes, which unfortunately cannot be distinguished. GRHL2 is well established as a nuclear protein (Zeng et al., Cancers 2024; Riethdorf et al., International Journal of Cancer 2015), and although PR is classically described as translocating to the nucleus upon hormone stimulation, several studies-including our own-have shown that PR is continuously present in the nucleus (Aarts et al., J Mammary Gland Biol Neoplasia 2023; Frigo et al., Essays Biochem. 2021).

We therefore propose that PR and GRHL2 may already interact in the nucleus without directly binding to chromatin. Given our observation that GRHL2 binding sites on the chromatin are redistributed upon R5020 mediated signaling activation, we hypothesize that such pre-formed PR-GRHL2 nuclear complexes may assist the rapid recruitment of GRHL2 to progesterone-responsive chromatin regions.

We have expanded the discussion to include a dedicated section addressing this point (line 376-388).

R2.13 It would be of interest to assess the overlap between the proteins identified in the RIME experiment and the motif analysis results.

In the discussion section of our original manuscript, we highlighted some overlapping proteins in the RIME and motif analysis, including STAT6 and FOXA1. However, we had not yet systematically analyzed overlap in both analyses. To address this, we now compared all enriched motifs (so not only the top 5 as displayed in our figures) under GRHL2, PR, and GRHL2/PR shared sites from both the CUT&RUN and ChIP-seq datasets with the proteins identified as GRHL2 interactors in our RIME. Although we identified numerous GRHL2-associated proteins, relatively few of them were transcription factors whose binding motifs were also enriched under GRHL2 peaks.

In our revised manuscript we have added a section in the discussion highlighting our systematic overlap of the results of our RIME experiment and the motif enrichment of the ChIP-seq and CUT&RUN analysis (line 415-436).

R2.14 The authors chose CUT&RUN to assess chromatin binding of PR and GRHL2. Given that RIME is also based on chromatin immunoprecipitation - ChIP protocol, it would be helpful to clarify why CUT&RUN was selected over ChIP-seq for the DNA-binding assays. What is the overlap with published data?

As also mentioned in our response to R1.3 and R1.5, we deliberately chose the CUT&RUN approach to minimize artifacts introduced by crosslinking and sonication, thereby reducing background and allowing the identification of high-confidence, direct DNA-binding events. Since GRHL2 physically interacts with PR, ChIP-seq could potentially capture indirect binding of GRHL2 at PR-bound sites (and vice versa). In contrast, CUT&RUN primarily detects direct DNA-protein interactions, providing a more specific and accurate binding profile. Additionally, CUT&RUN serves as an independent validation method for data obtained using ChIP-like protocols.

Since CUT&RUN, similar to ChIP, can show limited reproducibility (Nordin et al., Nucleic Acids Research, 2024), and to our knowledge few PR CUT&RUN and no GRHL2 CUT&RUN datasets are currently available, it is challenging to directly compare our data with published datasets. Nevertheless, studies performing PR or ER CUT&RUN (Gillis et al., Cancer Research, 2024; Reese et al., Molecular and Cellular Biology, 2022) report a comparable number of peaks-in the same range of thousands-as observed in our data. This suggests that a single CUT&RUN experiment in general may detect fewer events than a single ChIP-seq experiment, but that the peaks that are found are likely to reflect direct binding events.

Reviewer #2 (Significance (Required)):

General Assessment: This study investigates the role of the transcription factor GRHL2 in modulating PR function, using RIME and CUT&RUN to explore protein-protein and protein-chromatin interactions. GRHL2 have been implicated in epithelial biology and transcriptional regulation and interaction with steroid hormone receptors has been reported. This study extends the field by showing a functional link between GRHL2 and PR, which has implications for understanding hormone-dependent gene regulation.

The research will primarily interest a specialized audience in transcriptional regulation, chromatin biology, and hormone receptor signaling.

Key words for this reviewer: chromatin biology, transcription factor function, epigenomics, and proteomics.

We agree that with our implemented changes, this study should reach (and appeal to) an audience interested in transcriptional regulation, chromatin biology, hormone receptor signaling and breast cancer.

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

This study explores the important transcriptional coordination role of Grainyhead-like 2 (GRHL2) on the transcriptional regulatory function of progesterone receptor (PR). In this paper, the authors start with their recruitment characteristics, take into account their regulatory effects on downstream genes and their effects on the occurrence and development of breast cancer, and further clarify the coordination between them in three-dimensional space. The interaction between GRHL2 and PR, and the subsequent important influence on the co-regulated genes by GRHL2 and PR are analyzed. The overall framework of this study is mainly by RNA seq and CUT-TAG analysis, the molecular mechanism underlying the association between GRHL2 and PR and regulation function of two proteins in breast cancer is not clearly clarified. Some details need to be further improved：

Major comments: R3.1 For Fig.1D, the molecular weight of each protein should be marked in the diagram, and the expression of GRHL2 in the input group should be supplemented.

We apologize for not including molecular weights in our initial submission. We are not entirely clear what the reviewer means with their statement that "the expression of GRHL2 in the input group should be supplemented". The blot depicted in Figure 1D shows both the input signal and the IP. For the reviewer's information, the full Western blot is depicted below.

Figure 3 for reviewer: Full WBs of input and IP GRHL2 samples stained for GRHL2 or PR. NT = non-treated, T = treated

R3.2 In Fig.2B and Fig 5C, it should be describe well whether GRHL2 recruitment is in the absence or presence of R5020? How about the co-occupancy of PR and GRHL2 region, Promoter or enhancer region? It would be better to show histone marks such as H3K27ac and H3K4me1 to annotate the enhancer region.

As also stated in our response to R1.3, we acknowledge that the ChIP-seq experiments cannot definitively determine whether GRHL2 and PR co-occupy genomic regions under ligand-stimulated conditions, since the GRHL2 dataset was generated in the absence of progesterone stimulation (as indicated in lines 167-169). To clarify this, we have now specified this detail in the legend of figure 2 by noting "untreated GRHL2 ChIP." To directly assess GRHL2 chromatin binding under progesterone-stimulated conditions, we performed CUT&RUN experiments for both GRHL2 and PR under untreated and R5020-treated conditions. These experiments revealed a subset of overlapping PR and GRHL2 binding sites (approximately 5% of all identified PR peaks.

In our original manuscript, we performed genomic annotation of the GRHL2, PR, and GRHL2/PR overlapping peaks (Figure 2E) and found that most of these sites were located in intergenic regions, where enhancers are typically found, with ~20% located in promoter regions. We appreciate the reviewer's suggestion to further overlap the ChIP-seq peaks with histone marks such as H3K27ac and H3K4me1. We have now incorporated publicly available ATAC-seq and H3K27ac ChIP datasets in our revised manuscript (as also suggested by Reviewer 1) and find that shared GRHL2/PR sites are indeed located in active enhancer regions marked by H3K27ac (see Figure 2F). Additionally, as expected, we find that GRHL2/PR overlapping sites are enriched at open chromatin (Figure 2G).

R3.3 What is the biological function analysis by KEGG or GO analysis for the overlapping genes from VN plots of RNA-seq with CUT-TAG peaks. The genes co-regulated by GRH2L and PR are further determined.

For us, it is not entirely clear what reviewer 3 is asking here, but we can explain the following: as it is challenging to integrate HiChIP with CUT&RUN, due to the fundamentally different nature of the two techniques, we chose not to directly assign genes to CUT&RUN peaks. However, we did carefully link the GRHL2, PR, and GRHL2/PR ChIP-seq peaks to their target genes by integrating chromatin looping data from a PR HiChIP analysis. The result from this analysis is depicted in Figure 4B.

As suggested by this reviewer, we also performed a GO-term analysis on the 79 genes that are regulated by both GRHL2 and PR (we now have 79 genes after the re-analysis as suggested in R1.6). The corresponding results are provided for the reviewer in figure 3 of this rebuttal (below). As this additional analysis does not provide further biological insight beyond what is already presented in Figure 4C, we decided to not include this figure in the manuscript.

Figure 4 for reviewer: GO-term analysis on the 79 GRHL2-PR co-regulated genes that are transcriptionally regulated by GRHL2 and PR and that also harbor a PR HiChIP loop anchor at or near their TSS

R3.4 Western blotting should be performed to determine the protein levels of downstream genes co-regulated genes by GRH2L and PR in the absence or presence of R5020.

We agree that determining the response of co-regulated is important. Therefore, in Figure 4D, we present three representative examples of genes that are directly co-regulated by GRHL2 and PR-specifically, genes that are differentially expressed after 4 hours of R5020 exposure. Although protein levels of the targets are of functional importance, GRHL2 and PR are of transcription factors whose immediate effects are primarily exerted at the level of gene transcription. Therefore, in our opinion, changes in mRNA abundance provide the most direct and mechanistically relevant readout of their regulatory activity.

R3.5 The author mentioned that this study positions that GRHL2 acts as a crucial modulator of steroid hormone receptor function, while the authors do not provide the evidences that how does GRHL2 regulate PR-mediated transactivation, and how about these two proteins subcellular distribution in breast cancer cells.

We agree that while our RNA-seq data demonstrate that GRHL2 modulates the expression of PR target genes, and our CUT&RUN experiments show that GRHL2 chromatin binding is reshaped upon R5020 exposure, we have not yet further dissected the molecular mechanism by which GRHL2 functions as a PR co-regulator.

As also mentioned in our response to R1.2, we did consider several follow-up experiments to address this, including PR CUT&RUN in GRHL2 knockdown cells, CUT&RUN for known co-activators such as KMT2C/D and P300, as well as functional studies involving GRHL2 TAD and DBD mutants. However, due to technical and logistical challenges, we were unable to carry out these experiments within the timeframe of this study.

That said, we fully recognize that such approaches would provide deeper mechanistic insight into the interplay between PR and GRHL2. We have therefore explicitly acknowledged this limitation in our limitations of the study section (lines 502-507) and consider it an important avenue for future investigation.

Regarding the subcellular distribution in breast cancer cells: As also mentioned in our response to R2.12, GRHL2 is well established as a nuclear protein (Zeng et al., Cancers 2024; Riethdorf et al., International Journal of Cancer 2015), and although PR is classically described as translocating to the nucleus upon hormone stimulation, several studies-including our own-have shown that PR is continuously present in the nucleus (Aarts et al., J Mammary Gland Biol Neoplasia 2023; Frigo et al., Essays Biochem. 2021). Thus, both proteins mostly reside in the nucleus in breast (cancer) cells both in the absence and presence of hormone stimulation, but dynamic subcellular shuttling is likely to occur.

Minor comments: Please describe in more detail the relationship between PR and GRHL2 binding independent of the hormone in the discussion section.

As also mentioned in our response to R2.12, we have expanded the discussion to include a dedicated section addressing this point (lines 376-388).

Reviewer #3 (Significance (Required)):

Advance: Compare the study to existing published knowledge, it fills a gap. The authors provide RNA seq and CUT-TAG sequence analysis to show the recruitment of GRHL2 and PR and the co-regulated genes in the absence or presence of progesterone.

Audience: breast surgery will be interested, and the audiences will cover clinical and basic research.

My expertise is focused on the epigenetic modulation of steroid hormone receptors in the related cancers, such as breast cancer, prostate cancer, and endometrial carcinoma.

We agree that with our implemented changes, this study should reach (and appeal to) an audience interested in transcriptional regulation, chromatin biology, hormone receptor signaling and breast cancer.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review): 

The medicinal leech preparation is an amenable system in which to understand how the underlying cellular networks for locomotion function. A previously identified non-spiking neuron (NS) was studied and found to alter the mean firing frequency of a crawl-related motoneuron (DE-3), which fires during the contraction phase of crawling. The data are mostly solid. Identifying upstream neurons responsible for crawl motor patterning is essential for understanding how rhythmic behavior is controlled.

Review of Revision: 

On a positive note, the rationale for the study is clearer to me now after reading the authors' responses to both reviewers, but that information, as described in the authors' responses, is minimally incorporated into the current revised paper. Incorporating a discussion of previous work on the NS cell has, indeed, improved the paper. 

I suggested earlier that the paper be edited for clarity but not much text has been changed since the first draft. I will provide an example of the types of sentences that are confusing. The title of the paper is: "Phase-specific premotor inhibition modulates leech rhythmic motor output". Are the authors referring to the inhibition created by premotor neurons (e.g., on to the motoneurons) or the inhibition that the premotor neurons receive? 

In this case, this is an interesting ambiguity: NS is inhibited and that inhibition is directly transmitted to the motoneurons because both cells are electrically coupled.  We believe that the title does not disguise the findings conveyed by the manuscript.

I also find the paper still confusing with regard to the suggested "functional homology" with the vertebrate Renshaw cells. When the authors set up this expectation of homology (should be analogy) in the introduction and other sections of the paper, one would assume that the NS cell would be directly receiving excitation from a motoneuron (like DE-3) and, in turn, the motoneuron would then receive some sort of inhibitory input to regulate its firing frequency. Essentially, I have always viewed the Renshaw cells as nature's clever way to monitor the ongoing activity of a motoneuron while also providing recurrent feedback or "recurrent inhibition" to modify that cell's excitatory state. The authors present their initial idea below on line 62. Authors write: "These neurons are present as bilateral pairs in each segmental ganglion and are functional homologs of the mammalian Renshaw cells (Szczupak, 2014). These spinal cord cells receive excitatory inputs from motoneurons and, in turn, transmit inhibitory signals to the motoneurons (Alvarez and Fyffe, 2007)." 

We agree with Reviewer #2: the correct term is "analogous," not "homologous." Thanks for pointing this out. We changed the term throughout the text.

The Reviewer is also right in the appreciation of the role of Renshaw cells. NS plays exactly the role that the Reviewer expresses. The ONLY difference is that NS is inhibited by the motoneurons, and in turn transmits this inhibition to the motoneurons via the rectifying electrical junctions. Attending the confusion that our description caused in the Reviewer, we have modified the cited sentence accordingly now in lines 65-67.

Minor note:

I suggest re-writing this last sentence as "these" is confusing. Change to: 'In the spinal cord, Renshaw interneurons receive excitatory inputs from motoneurons and, in turn, transmit inhibitory signals to them (Alvarez and Fyffe, 2007).'] 

Please, see the changes mentioned above.

Furthermore, the authors note that (line 69 on): "In the context of this circuit the activity of excitatory motoneurons evokes chemically mediated inhibitory synaptic potentials in NS. Additionally, the NS neurons are electrically coupled......In physiological conditions this coupling favors the transmission of inhibitory signals from NS to motoneurons." Based on what is being conveyed here, I see a disconnect with the "functional homology" being presented earlier. I may be missing something, but the Renshaw analogy seems to be quite different compared to what looks like reciprocal inhibition in the leech. If the authors want to make the analogy to Renshaw cells clearer, then they should make a simple ball and stick diagram of the leech system and visually compare it to the Renshaw/motoneuron circuit with regard to functionality. This simple addition would help many readers. 

We have simplified the description regarding the Renshaw cell (lines 65-67) to avoid the “details” of the connectivity between the two circuits.

This report focuses on NS neurons and their role in crawling; we mention the analogy with Renshaw cells to widen the interest of the results. We do not think that making a special diagram to compare how the two neurons play a similar role via different connections among the players is useful in the context of this manuscript.

The Abstract, Authors write (line 19), "Specifically, we analyzed how electrophysiological manipulation of a premotor nonspiking (NS) neuron, that forms a recurrent inhibitory circuit (homologous to vertebrate Renshaw cells)...."

First, a circuit would not be homologous to a cell, and the term homology implies a strict developmental/evolutionary commonality. At best, I would use the term functionally analogous but even then I am still not sure that they are functionally that similar (see comments above). 

Reviewer #2 is right. We changed the sentence in line 20.

Line 22: "The study included a quantitative analysis of motor units active throughout the fictive crawling cycle that shows that the rhythmic motor output in isolated ganglia mirrors the phase relationships observed in vivo." This sentence must be revised to indicate that not all of the extracellular units were demonstrated to be motor units. Revise to: "The study included a quantitative analysis of identified and putative motor units active throughout the fictive crawling cycle that shows.....' 

Line 187 regarding identifying units as motoneurons: Authors write, "While multiple extracellular recordings have been performed previously (Eisenhart et al., 2000), these results (Figure 4) present the first quantitative analysis of motor units activated throughout the crawling cycle in this type of recordings." The authors cannot assume that the units in the recorded nerves belong only to motoneurons. Based on their first rebuttal, the authors seem to be reluctant to accept the idea that the extracellularly recorded units might represent a different class of neurons. They admit that some sensory neurons (with somata located centrally) do, indeed, travel out the same nerves recorded, but go on to explain why they would not be active. 

The leech has a variety of sensory organs that are located in the periphery, and some of these sensory neurons do show rhythmic activity correlated with locomotor activity (see Blackshaw's early work). The numerous stretch receptors, in fact, have very large axons that pass through all the nerves recorded in the current paper. 

In Fig. 4, it is interesting that the waveforms of all the units recorded in the PP nerve exhibit a reversal in waveform as compared to those in the DP nerve, which might indicate (based on bipolar differential recording) that the units in the PP nerve are being propagated in the opposite direction (i.e., are perhaps afferent). Rhythmic presynaptic inhibition and excitation is commonly seen for stretch receptors within the CNS (see the work of Burrows) and many such cells are under modulatory control. 

Most likely, the majority of the units are from motoneurons, but we do not really know at this point. The authors should reframe their statements throughout the paper as: 'While multiple extracellular recordings have been performed previously (Eisenhart et al., 2000), these results (Figure 4) present the first quantitative analysis of multiple extracellular units, using spike sorting methods, which are activated throughout the crawling cycle.' In cases where the identity of the unit is known, then it is fine to state that, but when the identity of the unit is not known, then there should be some qualification and stated as 'putative motor units' 

We understand the concern of Reviewer #2 regarding the type of neurons active during dopamine-induced crawling in isolated ganglia. However, we believe there is sufficient evidence to support that the recorded spikes originate from motoneurons. As readers may share the same concern, we have added a paragraph explaining why spikes from somatic sensory neurons such as P or T cells, or from stretch receptors, are unlikely to contribute (lines 206-214). We included the term putative in the abstract.

The Methods section:

Needs to include the full parameters that were used to assess whether bursting activity was qualified in ways to be considered crawling activity or not. Typically, crawl-like burst periods of no more than 25 seconds have been the limit for their qualification as crawling activity. In Fig 2F, for example, the inter-burst period is over 35 seconds; that coupled with an average 5 second burst duration would bring the burst period to 40 seconds, which is substantially out of range for there to be bursting relevant to crawl activity. Simply put, long DE-3 burst periods are often observed but may not be indicative of a crawl state as the CV motoneurons are no longer out of phase with DE-3. A number of papers have adopted this criterion. 

We now indicate in the methods the range of period values measured in our experiments.  For the reviewer informatio we show here histograms depicting the variability of period and duty cycle values recorded in our experiments (control conditions). The Reviewer can see that the bursting activity of DE-3 fall within what has been published.

Author response image 1.

Crawling in isolated ganglia. A. Histogram of periods end-to-end during crawling in isolated ganglia. The dotted line indicates the mean obtained from the averages of all experiments. The solid black line represents the mean of all cycles across all experiments. B. As in A, for the duty cycle calculated using end-to-end periods.  (n = 210 cycles from 45 ganglia obtained from 32 leeches in all cases).

Reviewer #1 (Recommendations for the authors): 

Minor comments-

Line 100: "In the frame of the recurrent inhibitory circuit, NS is the target of inhibitory signals". Suggestion: 'Within the framework of the recurrent inhibitory circuit, NS is the target of inhibitory signals.' 

Changed as suggested (line 107).

Line 163: "This series of experiments proves that, as predicted based on the known circuit (Figure 164 1C), inhibitory signals onto NS premotor neurons were transmitted to DE-3 motoneurons and counteracted their excitatory drive during crawling, limiting their firing frequency". I think this sentence is too strong plus needs some editing. Suggestion: 'As predicted based on the known circuit (Figure 164 1C), this series of experiments indicates that inhibitory signals onto NS premotor neurons are transmitted to DE-3 motoneurons, thus limiting their firing frequency and counteracting their excitatory drive during crawling."

Changed as suggested.

Lines 86, 292 and 304 and Fig 4 legend: "Different from DE-3, In-Phase units showed a marked decrease in the maximum bFF along time." Suggestion: Replace the word "along" with 'across' time. Also replace those words in the Fig 4 legend and Line 80...."along" (replace with 'across') the different stages of crawling. 

Changed as suggested.

Line 311: "bursts and a concurrent inhibitory input via NS (Figure 7). Coherent with this interpretation, the activity level of the Anti- Phase units was not influenced by these inhibitory signals". Suggestion: Replace the word "coherent" with 'consistent'. 

Changed as suggested.

Line 332: "...offer the particular advantage of allowing electrical manipulation of individual neurons in wildtype adults," I am unsure what the authors are attempting to convey. Not sure what they mean by "wildtype" in this context and why that would matter. 

“wildtype” was eliminated

We thank Reviewer #2 for the suggested edits to the text.

Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

This study advances the lab's growing body of evidence exploring higher-order learning and its neural mechanisms. They recently found that NMDA receptor activity in the perirhinal cortex was necessary for integrating stimulus-stimulus associations with stimulus-shock associations (mediated learning) to produce preconditioned fear, but it was not necessary for forming stimulus-shock associations. On the other hand, basolateral amygdala NMDA receptor activity is required for forming stimulus-shock memories. Based on these facts, the authors assessed: (1) why the perirhinal cortex is necessary for mediated learning but not direct fear learning, and (2) the determinants of perirhinal cortex versus basolateral amygdala necessity for forming direct versus indirect fear memories. The authors used standard sensory preconditioning and variants designed to manipulate the novelty and temporal relationship between stimuli and shock and, therefore, the attentional state under which associative information might be processed. Under experimental conditions where information would presumably be processed primarily in the periphery of attention (temporal distance between stimulus/shock or stimulus pre-exposure), perirhinal cortex NMDA receptor activation was required for learning indirect associations. On the other hand, when information would likely be processed in focal attention (novel stimulus contiguous with shock), basolateral amygdala NMDA activity was required for learning direct associations. Together, the findings indicate that the perirhinal cortex and basolateral amygdala subserve peripheral and focal attention, respectively. The authors provide support for their conclusions using careful, hypothesis-driven experimental design, rigorous methods, and integrating their findings with the relevant literature on learning theory, information processing, and neurobiology. Therefore, this work will be highly interesting to several fields.

Strengths:

(1) The experiments were carefully constructed and designed to test hypotheses that were rooted in the lab's previous work, in addition to established learning theory and information processing background literature.

(2) There are clear predictions and alternative outcomes. The provided table does an excellent job of condensing and enhancing the readability of a large amount of data.

(3) In a broad sense, attention states are a component of nearly every behavioral experiment. Therefore, identifying their engagement by dissociable brain areas and under different learning conditions is an important area of research.

(4) The authors clearly note where they replicated their own findings, report full statistical measures, effect sizes, and confidence intervals, indicating the level of scientific rigor.

(5) The findings raise questions for future experiments that will further test the authors' hypotheses; this is well discussed.

Weaknesses:

As a reader, it is difficult to interpret how first-order fear could be impaired while preconditioned fear is intact; it requires a bit of "reading between the lines".

We appreciate the Reviewer’s point and have attempted to address on lines 55-63 of the revised paper: “In a recent pair of studies, we extended these findings in two ways. First, we showed that S1 does not just form an association with shock in stage 2; it also mediates an association between S2 and the shock. Thus, S2 enters testing in stage 3 already conditioned, able to elicit fear responses (Wong et al., 2019). Second, we showed that this mediated S2-shock association requires NMDAR-activation in the PRh, as well as communication between the PRh and BLA (Wong et al., 2025). These findings raise two critical questions: 1) why is the PRh engaged for mediated conditioning of S2 but not for direct conditioning of S1; and 2) more generally, what determines whether the BLA and/or PRh is engaged for conditioning of the S1 and/or S2?”

Reviewer #2 (Public review):

Summary:

This paper continues the authors' research on the roles of the basolateral amygdala (BLA) and the perirhinal cortex (PRh) in sensory preconditioning (SPC) and second-order conditioning (SOC). In this manuscript, the authors explore how prior exposure to stimuli may influence which regions are necessary for conditioning to the second-order cue (S2). The authors perform a series of experiments which first confirm prior results shown by the author - that NMDA receptors in the PRh are necessary in SPC during conditioning of the first-order cue (S1) with shock to allow for freezing to S2 at test; and that NMDA receptors in the BLA are necessary for S1 conditioning during the S1-shock pairings. The authors then set out to test the hypothesis that the PRh encodes associations in a peripheral state of attention, whereas the BLA encodes associations in a focal state of attention, similar to the A1 and A2 states in Wagner's theory of SOP. To do this, they show that BLA is necessary for conditioning to S2 when the S2 is first exposed during a serial compound procedure - S2-S1-shock. To determine whether pre-exposure of S2 will shift S2 to a peripheral focal state, the authors run a design in which S2-S1 presentations are given prior to the serial compound phase. The authors show that this restores NMDA receptor activity within the PRh as necessary for the fear response to S2 at test. They then test whether the presence of S1 during the serial compound conditioning allows the PRh to support the fear responses to S2 by introducing a delay conditioning paradigm in which S1 is no longer present. The authors find that PRh is no longer required and suggest that this is due to S2 remaining in the primary focal state.

Strengths:

As with their earlier work, the authors have performed a rigorous series of experiments to better understand the roles of the BLA and PRh in the learning of first- and second-order stimuli. The experiments are well-designed and clearly presented, and the results show definitive differences in functionality between the PRh and BLA. The first experiment confirms earlier findings from the lab (and others), and the authors then build on their previous work to more deeply reveal how these regions differ in how they encode associations between stimuli. The authors have done a commendable job of pursuing these questions.

Table 1 is an excellent way to highlight the results and provide the reader with a quick look-up table of the findings.

Weaknesses:

The authors have attempted to resolve the question of the roles of the PRh and BLA in SPC and SOC, which the authors have explored in previous papers. Laudably, the authors have produced substantial results indicating how these two regions function in the learning of first- and second-order cues, providing an opportunity to narrow in on possible theories for their functionality. Yet the authors have framed this experiment in terms of an attentional framework and have argued that the results support this particular framework and hypothesis - that the PRh encodes peripheral and the BLA encodes focal states of learning. This certainly seems like a viable and exciting hypothesis, yet I don't see why the results have been completely framed and interpreted this way. It seems to me that there are still some alternative interpretations that are plausible and should be included in the paper.

We appreciate the Reviewer’s point and have attempted to address it on lines 566-594 of the Discussion: “An additional point to consider in relation to Experiments 3A, 3B, 4A and 4B is the level of surprise that rats experienced following presentations of the familiar S2 in stage 2. Specifically, in Experiments 3A and 3B, S2 was followed by the expected S1 (low surprise) and its conditioning required activation of NMDA receptors in the PRh and not the BLA. By contrast, in Experiments 4A and 4B, S2 was followed by omission of the expected S1 (high surprise) and its conditioning required activation of NMDA receptors in the BLA and not the PRh. This raises the possibility that surprise, or prediction error, also influences the way that S2 is processed in focal and peripheral states of attention. When prediction error is low, S2 is processed in the peripheral state of attention: hence, learning under these circumstances requires NMDA receptor activation in the PRh and not the BLA. By contrast, when prediction error is high, S2 is preserved in the focal state of attention: hence, learning under these circumstances requires NMDA receptor activation in the BLA and not the PRh. The impact of prediction error on the processing of S2 could be assessed using two types of designs. In the first design, rats are pre-exposed to S2-S1 pairings in stage 1 and this is followed by S2-S3-shock pairings in stage 2. The important feature of this design is that, in stage 2, the S2 is followed by surprise in omission of S1 and presentation of S3. Thus, if a large prediction error maintains processing of the familiar S2 in the BLA, we might expect that its conditioning in this design would require NMDA receptor activation in the BLA (in contrast to the results of Experiment 3B) and no longer require NMDA receptor activation in the PRh (in contrast to the results of Experiment 3A). In the second design, rats are pre-exposed to S2 alone in stage 1 and this is followed by S2-[trace]-shock pairings in stage 2. The important feature of this design is that, in stage 2, the S2 is not followed by the surprising omission of any stimulus. Thus, if a small prediction error shifts processing of the familiar S2 to the PRh, we might expect that its conditioning in this design would no longer require NMDA receptor activation in the BLA (in contrast to the results of Experiment 4B) but, instead, require NMDA receptor activation in the PRh (in contrast to the results of Experiment 4A). Future studies will use both designs to determine whether prediction error influences the processing of S2 in the focus versus periphery of attention and, thereby, whether learning about this stimulus requires NMDA receptor activation in the BLA or PRh.”

Reviewer #3 (Public review):

Summary:

This manuscript presents a series of experiments that further investigate the roles of the BLA and PRH in sensory preconditioning, with a particular focus on understanding their differential involvement in the association of S1 and S2 with shock.

Strengths:

The motivation for the study is clearly articulated, and the experimental designs are thoughtfully constructed. I especially appreciate the inclusion of Table 1, which makes the designs easy to follow. The results are clearly presented, and the statistical analyses are rigorous. My comments below mainly concern areas where the writing could be improved to help readers more easily grasp the logic behind the experiments.

Weaknesses:

(1) Lines 56-58: The two previous findings should be more clearly summarized. Specifically, it's unclear whether the "mediated S2-shock" association occurred during Stage 2 or Stage 3. I assume the authors mean Stage 2, but Stage 2 alone would not yet involve "fear of S2," making this expression a bit confusing.

We apologise for the confusion and have revised the summary of our previous findings on lines 55-63. The revised text now states: “In a recent pair of studies, we extended these findings in two ways. First, we showed that S1 does not just form an association with shock in stage 2; it also mediates an association between S2 and the shock. Thus, S2 enters testing in stage 3 already conditioned, able to elicit fear responses (Wong et al., 2019). Second, we showed that this mediated S2-shock association requires NMDAR-activation in the PRh, as well as communication between the PRh and BLA (Wong et al., 2025). These findings raise two critical questions: 1) why is the PRh engaged for mediated conditioning of S2 but not for direct conditioning of S1; and 2) more generally, what determines whether the BLA and/or PRh is engaged for conditioning of the S1 and/or S2?”

(2) Line 61: The phrase "Pavlovian fear conditioning" is ambiguous in this context. I assume it refers to S1-shock or S2-shock conditioning. If so, it would be clearer to state this explicitly.

Apologies for the ambiguity - we have omitted the term “Pavlovian” which may have been the source of confusion: The revised text on lines 60-63 now states: “These findings raise two critical questions: 1) why is the PRh engaged for mediated conditioning of S2 but not for direct conditioning of S1; and 2) more generally, what determines whether the BLA and/or PRh is engaged for conditioning of the S1 and/or S2?”

(3) Regarding the distinction between having or not having Stage 1 S2-S1 pairings, is "novel vs. familiar" the most accurate way to frame this? This terminology could be misleading, especially since one might wonder why S2 couldn't just be presented alone on Stage 1 if novelty is the critical factor. Would "outcome relevance" or "predictability" be more appropriate descriptors? If the authors choose to retain the "novel vs. familiar" framing, I suggest providing a clear explanation of this rationale before introducing the predictions around Line 118.

We have incorporated the suggestion regarding “predictability” while also retaining “novelty” as follows. 

L76-85: “For example, different types of arrangements may influence the substrates of conditioning to S2 by influencing its novelty and/or its predictive value at the time of the shock, on the supposition that familiar stimuli are processed in the periphery of attention and, thereby, the PRh (Bogacz & Brown, 2003; Brown & Banks, 2015; Brown & Bashir, 2002; Martin et al., 2013; McClelland et al., 2014; Morillas et al., 2017; Murray & Wise, 2012; Robinson et al., 2010; Suzuki & Naya, 2014; Voss et al., 2009; Yang et al., 2023) whereas novel stimuli are processed in the focus of attention and, thereby, the amygdala (Holmes et al., 2018; Qureshi et al., 2023; Roozendaal et al., 2006; Rutishauser et al., 2006; Schomaker & Meeter, 2015; Wright et al., 2003).”

L116-120: “Subsequent experiments then used variations of this protocol to examine whether the engagement of NMDAR in the PRh or BLA for Pavlovian fear conditioning is influenced by the novelty/predictive value of the stimuli at the time of the shock (second implication of theory) as well as their distance or separation from the shock (third implication of theory; Table 1).”

(4) Line 121: This statement should refer to S1, not S2.

(5) Line 124: This one should refer to S2, not S1.

We have checked the text on these lines for errors and confirmed that the statements are correct. The lines encompassing this text (L121-130) are reproduced here for convenience:

(1) When rats are exposed to novel S2-S1-shock sequences, conditioning of S2 and S1 will be disrupted by a DAP5 infusion into the BLA but not into the PRh (Experiments 2A and 2B);

(2) When rats are exposed to S2-S1 pairings and then to S2-S1-shock sequences, conditioning of S2 will be disrupted by a DAP5 infusion into the PRh but not the BLA whereas conditioning of S1 will be disrupted by a DAP5 infusion into the BLA not the PRh (Experiments 3A and 3B);

(3) When rats are exposed to S2-S1 pairings and then to S2 (trace)-shock pairings, conditioning of S2 will be disrupted by a DAP5 into the BLA not the PRh (Experiments 4A and 4B).

(6) Additionally, the rationale for Experiment 4 is not introduced before the Results section. While it is understandable that Experiment 4 functions as a follow-up to Experiment 3, it would be helpful to briefly explain the reasoning behind its inclusion.

Experiment 4 follows from the results obtained in Experiment 3; and, as noted, the reasoning for its inclusion is provided locally in its introduction. We attempted to flag this experiment earlier in the general introduction to the paper; but this came at the cost of clarity to the overall story. As such, our revised paper retains the local introduction to this experiment. It is reproduced here for convenience:

“In Experiments 3A and 3B, conditioning of the pre-exposed S1 required NMDAR-activation in the BLA and not the PRh; whereas conditioning of the pre-exposed S2 required NMDAR-activation in the PRh and not the BLA. We attributed these findings to the fact that the pre-exposed S2 was separated from the shock by S1 during conditioning of the S2-S1-shock sequences in stage 2: hence, at the time of the shock, S2 was no longer processed in the focal state of attention supported by the BLA; instead, it was processed in the peripheral state of attention supported by the PRh.

“Experiments 4A and 4B employed a modification of the protocol used in Experiments 3A and 3B to examine whether a pre-exposed S1 influences the processing of a pre-exposed S2 across conditioning with S2-S1-shock sequences. The design of these experiments is shown in Figure 4A. Briefly, in each experiment, two groups of rats were exposed to a session of S2-S1 pairings in stage 1 and, 24 hours later, a session of S2-[trace]-shock pairings in stage 2, where the duration of the trace interval was equivalent to that of S1 in the preceding experiments. Immediately prior to the trace conditioning session in stage 2, one group in each experiment received an infusion of DAP5 or vehicle only into either the PRh (Experiment 4A) or BLA (Experiment 4B). Finally, all rats were tested with presentations of the S2 alone in stage 3. If the substrates of conditioning to S2 are determined only by the amount of time between presentations of this stimulus and foot shock in stage 2, the results obtained in Experiments 4A and 4B should be the same as those obtained in Experiments 3A and 3B: acquisition of freezing to S2 will require activation of NMDARs in the PRh and not the BLA. If, however, the presence of S1 in the preceding experiments (Experiments 3A and 3B) accelerated the rate at which processing of S2 transitioned from the focus of attention to its periphery, the results obtained in Experiments 4A and 4B will differ from those obtained in Experiments 3A and 3B. That is, in contrast to the preceding experiments where acquisition of freezing to S2 required NMDAR-activation in the PRh and not the BLA, here acquisition of freezing to S2 should require NMDAR-activation in the BLA but not the PRh.”

Reviewer #1 (Recommendations for the authors):

I greatly enjoyed reading and reviewing this manuscript, and so I only have boilerplate recommendations.

(1) I might add a couple of sentences discussing how/why preconditioned fear could be intact while first-order fear is impaired. Of course, if I am interpreting the provided interpretation correctly, the reason is that peripheral processing is still intact even when BLA NMDA receptors are blocked, and so mediated conditioning still occurs. Does this mean that mediated conditioning does not require learning the first-order relationship, and that they occur in parallel? Perhaps I just missed this, but I cannot help but wonder whether/how the psychological processes at play might change when first-order learning is impaired, so this would be greatly appreciated.

As noted above, we have revised the general introduction (around lines 55-59) to clarify that the direct S1-shock and mediated S2-shock associations form in parallel. Hence, manipulations that disrupt first-order fear to the S1 (such as a BLA infusion of the NMDA receptor antagonist, DAP5) do not automatically disrupt the expression of sensory preconditioned fear to the S2.

(2) Adding to the above - does the SOP or another theory predict serial vs parallel information flow from focal state to peripheral, or perhaps it is both to some extent?

SOP predicts both serial and parallel processing of information in its focal and peripheral states. That is, some proportion of the elements that comprise a stimulus may decay from the focal state of attention to the periphery (serial processing); hence, at any given moment, the elements that comprise a stimulus can be represented in both focal and peripheral states (parallel processing).

Given the nature of the designs and tools used in the present study (between-subject assessment of a DAP5 effect in the BLA or PRh), we selected parameters that would maximize the processing of the S2 and S1 stimuli in one or the other state of activation; hence the results of the present study. We are currently examining the joint processing of stimulus elements across focal and peripheral states using simultaneous recordings of activity in the BLA and PRh. These recordings are collected from rats trained in the different stages of a within-subject sensory preconditioning protocol. The present study created the basis for this work, which will be published separately in due course.

(3) The organization of PRh vs BLA is nice and consistent across each figure, but I would suggest adding any kind of additional demarcation beyond the colors and text, maybe just more space between AB / CD. The figure text indicating PRh/BLA is a bit small.

Thank you for the suggestion – we have added more space between the top and bottom panels of the figure.

(4) Line 496 typo ..."in the BLA but not the BLA".

Apologies for the type - this has been corrected.

Reviewer #2 (Recommendations for the authors):

I found the experiments to be extremely well-designed and the results convincing and exciting. The hypothesis of the focal and peripheral states of attention being encoded by BLA and PRh respectively, is enticing, yet as indicated in the public review, this does not seem to be the only possible interpretation. This is my only serious comment for the authors.

(1) I think it would be worth reframing the article slightly to give credence to alternative hypotheses. Not to say that the authors' intriguing hypothesis shouldn't be an integral part of the introduction, but no alternatives are mentioned. In experiment 2, could the fact that S2 is already being a predictor of S1, not block new learning to S2? In the framework of stimulus-stimulus associations, there would be no surprise in the serial-compound stage of conditioning at the onset of S1. This may prevent direct learning of the S2-shock association within the BLA. This type of association may as well (S2 predicts S1, but it's omitted), which could support learning by S2. fall under the peripheral/focal theory, but I don't think it's necessary to frame this possibility in terms of a peripheral/focal theory. To build on this alternative interpretation, the absence of S1 in experiment 4 may induce a prediction error. The peripheral and focal states appear to correspond to A2 and A1 in SOP extremely well, and I think it would potentially add interest and support. If the authors do intend to make the paper a strong argument for their hypothesis, perhaps a few additional experiments may be introduced. If the novelty of S2 is critical for S2 not to be processed in a focal state during the serial compound stage, could pre-exposure of S2 alone allow for dependence of S2-shock on the PRh? Assuming this is what the authors would predict, this might disentangle the S-S theory mentioned above from the peripheral/focal theory. Or perhaps run an experiment S2-X in stage 1 and S2-S1-shock in stage 2? This said, I think the experiments are more than sufficient for an exciting paper as is, and I don't think running additional experiments is necessary. I would only argue for this if the authors make a hard claim about the peripheral/focal theory, as is the case for the way the paper is currently written.

We appreciate the reviewer’s excellent point and suggestions. We have included an additional paragraph in the Discussion on page 24 (lines 566-594).  “An additional point to consider in relation to Experiments 3A, 3B, 4A and 4B is the level of surprise that rats experienced following presentations of the familiar S2 in stage 2. Specifically, in Experiments 3A and 3B, S2 was followed by the expected S1 (low surprise) and its conditioning required activation of NMDA receptors in the PRh and not the BLA. By contrast, in Experiments 4A and 4B, S2 was followed by omission of the expected S1 (high surprise) and its conditioning required activation of NMDA receptors in the BLA and not the PRh. This raises the possibility that surprise, or prediction error, also influences the way that S2 is processed in focal and peripheral states of attention. When prediction error is low, S2 is processed in the peripheral state of attention: hence, learning under these circumstances requires NMDA receptor activation in the PRh and not the BLA. By contrast, when prediction error is high, S2 is preserved in the focal state of attention: hence, learning under these circumstances requires NMDA receptor activation in the BLA and not the PRh. The impact of prediction error on the processing of S2 could be assessed using two types of designs. In the first design, rats are pre-exposed to S2-S1 pairings in stage 1 and this is followed by S2-S3-shock pairings in stage 2. The important feature of this design is that, in stage 2, the S2 is followed by surprise in omission of S1 and presentation of S3. Thus, if a large prediction error maintains processing of the familiar S2 in the BLA, we might expect that its conditioning in this design would require NMDA receptor activation in the BLA (in contrast to the results of Experiment 3B) and no longer require NMDA receptor activation in the PRh (in contrast to the results of Experiment 3A). In the second design, rats are pre-exposed to S2 alone in stage 1 and this is followed by S2-[trace]-shock pairings in stage 2. The important feature of this design is that, in stage 2, the S2 is not followed by the surprising omission of any stimulus. Thus, if a small prediction error shifts processing of the familiar S2 to the PRh, we might expect that its conditioning in this design would no longer require NMDA receptor activation in the BLA (in contrast to the results of Experiment 4B) but, instead, require NMDA receptor activation in the PRh (in contrast to the results of Experiment 4A). Future studies will use both designs to determine whether prediction error influences the processing of S2 in the focus versus periphery of attention and, thereby, whether learning about this stimulus requires NMDA receptor activation in the BLA or PRh.”

(3) I was surprised the authors didn't frame their hypothesis more in terms of Wagner's SOP model. It was minimally mentioned in the introduction or the authors' theory if it were included more in the introduction. I was wondering whether the authors may have avoided this framing to avoid an expectation for modeling SOP in their design. If this were the case, I think the paper stands on its own without modeling, and at least for myself, a comparison to SOP would not require modeling of SOP. If this was the authors' concern for avoiding it, I would suggest to the authors that they need not be concerned about it.

We appreciate the endorsement of Wagner’s SOP theory as a nice way of framing our results. We are currently working on a paper in which we use simulations to show how Wagner’s theory can accommodate the present findings as well as others in the literature on sensory preconditioning. For this reason, we have not changed the current paper in relation to this point.

Author response:

Reviewer #1 (Public review)

I have to preface my evaluation with a disclosure that I lack the mathematical expertise to fully assess what seems to be the authors' main theoretical contribution. I am providing this assessment to the best of my ability, but I cannot substitute for a reviewer with more advanced mathematical/physical training.

Summary:

This paper describes a new theoretical framework for measuring parsimony preferences in human judgments. The authors derive four metrics that they associate with parsimony (dimensionality, boundary, volume, and robustness) and measure whether human adults are sensitive to these metrics. In two tasks, adults had to choose one of two flower beds which a statistical sample was generated from, with or without explicit instruction to choose the flower bed perceptually closest to the sample. The authors conduct extensive statistical analyses showing that humans are sensitive to most of the derived quantities, even when the instructions encouraged participants to choose only based on perceptual distance. The authors complement their study with a computational neural network model that learns to make judgments about the same stimuli with feedback. They show that the computational model is sensitive to the tasks communicated by feedback and only uses the parsimony-associated metrics when feedback trains it to do so.

Strengths:

(1)  The paper derives and applies new mathematical quantities associated with parsimony. The mathematical rigor is very impressive and is much more extensive than in most other work in the field, where studies often adopt only one metric (such as the number of causes or parameters). These formal metrics can be very useful for the field.

(2)  The studies are preregistered, and the statistical analyses are strong.

(3)  The computational model complements the behavioral findings, showing that the derived quantities are not simply equivalent to maximum-likelihood inference in the task.

(4)  The speculations in the discussion section (e.g., the idea that human sensitivity is driven by the computational demands each metric requires) are intriguing and could usefully guide future work.

Weaknesses:

(1) The paper is very hard to understand. Many of the key details of the derived metrics are in the appendix, with very little accessible explanation in the main text. The figures helped me understand the metrics somewhat, although I am still not sure how some of them (such as boundary or robustness as measured here) are linked to parsimony. I understand that this is addressed by the derivations in the appendix, but as a computational cognitive scientist, I would have benefited from more accessible explanations. Important aspects of the human studies are also missing from the main text, such as the sample size for Experiment 2.

(2) It is not fully clear whether the sensitivity of human participants to some of the quantities convincingly reported here actually means that participants preferred shapes according to the corresponding aspect of parsimony. The title and framing suggest that parsimony "guides" human decision-making, which may lead readers to conclude that humans prefer more parsimonious shapes. I am not sure the sensitivity findings alone support this framing, but it might just be my misunderstanding of the analyses.

(3) The stimulus set included only four combinations of shapes, each designed to diagnostically target one of the theoretical quantities. It is unclear whether the results are robust or specific to these particular 4 stimuli.

(4) The study is framed as measuring "decision-making," but the task resembles statistical inference (e.g., which shape generated the data) or perceptual judgment. This is a minor point since "decision-making" is not well defined in the literature, yet the current framing in the title gave me the initial impression that humans would be making preference choices and learning about them over time with feedback.