Reviewer #1 (Public review):

Summary:

This study examines whether gaze direction actively shapes choice during food preference decisions or whether gaze and choice evolve largely independently until the moment of commitment. The established framework in this context, the aDDM, assumes that gaze causally biases the accumulation of evidence in favour of the fixated item. The authors show convincingly that this model fails to fit key behavioural patterns across several datasets, as do other published models that make the same assumption. The authors propose an alternative model (Post-Decision-Gaze or PDG) in which gaze and decision formation are decoupled: gaze does not influence the decision process, nor is it drawn toward the ultimately chosen item, until after the decision threshold is reached. Only during the motor execution period (after commitment) is gaze directed to the chosen option. They demonstrate that this model fits several observed patterns better than the aDDM and related variants.

Strengths:

The work thoroughly considers multiple models and datasets. It advances an interesting alternative perspective on gaze-decision interactions and highlights meaningful shortcomings in existing models. The authors take the time to explain how modelling assumptions produce specific patterns in the data, which is certainly insightful to readers interested in the modelling of value-based decision making.

Weaknesses:

It is unclear to what extent the model's success relies on the way non-decision time is formalised in the model. In the proposed PDG model, non-decision time is decomposed into separate visual encoding, saccadic execution, and manual execution components. Several values (assumed or recovered) do not match known physiological or behavioural ranges. This is a common issue in the literature, and the authors may want to address it in light of broader work discussing what non-decision time consists of in both manual and saccadic actions (e.g., Bompas et al., 2024, Non decision time: the Higgs boson of decision, Psychological Review).

In particular, the "saccadic execution" parameter appears far too long and too variable to reflect merely execution; instead, it likely includes decisional components. This would make more sense since manual and saccadic planning essentially rely on distinct brain areas, hence it seems unrealistic that crossing a single threshold would trigger both manual and saccadic execution. Similarly, recovered manual non-decision times are substantially longer (though not more variable) than expected motor execution durations for button presses. These patterns suggest that parts of what the model treats as non-decision time are likely decisional in nature, although perhaps related to "action decision" rather than the "value-based decision" of interest to the authors. To what extent these two processes neatly follow each other or overlap could be usefully considered.

Reviewer #2 (Public review):

Summary:

Zylberberg et al. reanalyze eye-tracking and behavioral data (mostly from Krajbich et al., 2010) to test two predictions of the attentional Drift Diffusion Model, finding that these predictions are not met. Similarly, predictions of normative models (inspired by rational inattention) are not in line with the data, and the authors propose a post-choice model of attention. This model better accounts for the two effects but also does not account for all patterns, so the authors conclude that eye movements most likely reflect both pre- and post-decisional processes.

Strengths:

A clear strength is the systematic falsification-based approach of the paper, establishing (partially) new predictions and testing to what extent these are met by extant models and by a newly developed theory. The authors do a good job in providing intuitions behind the effects and the reasons why models such as the aDDM predict them. The paper is of substantial relevance for the field, as it shows that effects pertaining to the last fixation(s) should be interpreted with caution. Another strength is the paper's transparency as the authors clearly acknowledge that their new model does not do a perfect job either.

Weaknesses:

The paper focuses on analyzing the Krajbich 2010 data, but shows that the second effect replicates in many other datasets. A more principled approach, in which both effects are analyzed and presented for all datasets, would be more convincing. The results should then be shown together for clarity/readability.

Similarly, it would be nice to show to what extent the models' predictions depend (not depend) on using the best-fitting parameter values (are there any parameter settings under which the two effects are not predicted?)

Reviewer #3 (Public review):

Summary:

In this study, the authors reanalyzed choice, RT and gaze datasets collected from human subjects performing a food-choice task. They show that models that posit a causal role for attention in shaping the decision-making process fail to account for empirical observations in the data. These include the attentional drift diffusion model (aDDM) and models that derive attention-choice associations from an optimal policy. The authors show that a model that assumes that gazes are directed towards the chosen option after decision commitment captures more (but not all) empirical findings, suggesting that attention may reflect decisions once they are made instead of contributing to their formation. However, this post-decision-gaze (PDG) model failed to capture all aspects of the data, suggesting that gaze may reflect both decisional and post-decisional operations, and existing models are still missing some features of the gaze-directing process. The authors provide convincing evidence that post-decision gaze explains a number of empirical findings in this task.

Strengths:

(1) The analyses are generally appropriate, and the conclusions are supported by the data.

(2) The study was rigorous, as the authors considered a number of alternative possible models for behavior, and evaluated their performance based on a wide range of qualitative predictions (as opposed to exclusively relying on model comparison).

(3) The proposal that gaze may largely reflect post-decisional processes is interesting, and as far as I am aware, novel.

Weaknesses:

There was limited discussion about why one might allocate attention post-decision. I would have appreciated more discussion on the potential functional consequences or implications of post-decision gaze.

eLife Assessment

This study provides a valuable contribution to understanding grid-to-place transformations, offering new insights into the structure and reliability of these representations and extending prior work in a meaningful way. The evidence supporting the authors' conclusions is solid, based on careful analyses and well-executed experiments, although clarity and mechanistic interpretation would be strengthened by improving sample size reporting, expanding population-level analyses, and future studies including simultaneous entorhinal-hippocampal recordings. The work will be of interest to neuroscientists studying spatial coding and hippocampal-entorhinal circuit function.

Reviewer #1 (Public review):

This manuscript investigates how chemogenetic depolarization of medial entorhinal cortex layer II stellate cells reshapes spatial coding in downstream hippocampal CA1. Building on the authors' prior work (Kanter et al., Neuron 2017), the study examines changes in grid cell subfield firing rates and CA1 place cell firing patterns after CNO administration. A central advance of the present work is the use of the same manipulation on two consecutive days. The authors show that the induced grid subfield rate changes are highly similar across days and that CA1 place field reorganization is likewise reproducible across days. In addition, they report that CA1 remapping after CNO is not arbitrary. The new main place field often emerges at a location that can be anticipated from the baseline rate map of the same cell, typically corresponding to a weak secondary peak outside the primary field. Finally, the authors demonstrate that these experimental findings can be recapitulated in a feedforward grid to place cell model by selectively redistributing grid subfield firing rates, supporting the interpretation that grid subfield rate changes are sufficient to drive predictable and reproducible place field reorganization.

Overall, this study is positioned as a follow-up to the authors' previous report in which the main phenomenon (grid subfield rate remapping and accompanying CA1 place cell remapping following chemogenetic depolarization of MEC layer II neurons) was already established. While the conceptual novelty is therefore incremental, the present manuscript adds important and convincing evidence about two key properties of this phenomenon, including its reproducibility across days and the extent to which the direction of place field reorganization is predictable from baseline activity. The experimental approach and analyses appear generally appropriate and carefully executed, and the inclusion of modeling strengthens the mechanistic interpretation. These results provide useful new insight into stable input-output relationships within the entorhinal hippocampal system, and the work will be of interest to researchers studying remapping and the grid to place cell transformation.

Reviewer #2 (Public review):

Summary:

Hippocampal remapping - the collective reorganization of neural tuning properties - is thought to be a crucial determinant of memory outcomes. Understanding its mechanistic bases is a fundamental goal of neuroscience and likely to be critical to understanding memory in health and disease. Here, Lykken et al. 2025 leverage a unique empirical manipulation paired with computational modeling to investigate how one mechanism - reorganization of grid cell subfield firing rates - impacts hippocampal remapping. The authors find that repeated chemogenetic excitation of MEC stellate cells induces reliable reorganization of grid cell subfield firing rates, which is in turn coupled with reliable hippocampal remapping. Notably, the authors show that this hippocampal remapping is not random but predictable, with changes in field location that can be predicted based on weak out-of-field firing observed during control sessions. These findings were well-replicated by a simple model of grid-to-place transformation.

Strengths:

This work has many strengths. One key strength of this work is its compelling demonstration that chemogenetic activation of stellate cells induces changes to the grid and place cell representations, which are reliable across repeated activations. This reliability means that the functional changes induced by this manipulation are not merely noise but rather contain a consistent structure that can be investigated to gain insight into the entorhinal-hippocampal transformation. Similarly, the demonstration that hippocampal remapping during this manipulation is not random, but predictable at the single-cell level, is also a strength. This predictability can help us distinguish competing mechanisms of remapping and place field formation more generally. Finally, by reproducing key experimental outcomes with a straightforward grid-to-place computational model, the authors show that this relatively simple model is sufficient to understand their results.

Weaknesses:

This work also has limitations that leave some relevant questions open at this time. One such set of questions which might be addressable with the author's data and modeling concerns population analyses. Do grid fields at similar locations exhibit similar changes in field properties, or do these fields change independently? Are changes in field location consistent or inconsistent among simultaneously recorded place cells? Would we expect or not expect such a structure given the model? These results might help discriminate between different mechanisms possibly at play.

Another limitation of this work is its reliance on a single measure of predictability. While this is a great start, and the various controls and modeling are appreciated, I wonder whether the modeling could be used to generate additional verifiable predictions. For example, perhaps analyzing whether there is or is not structure to unpredictable errors (are these distributed around predictions but further away, or are they random)?

Finally, one limitation comes from the between-group nature of the recordings. Because the MEC and hippocampus are recorded in separate groups of animals, the authors lose the ability to test whether each mouse's particular grid field reorganization predicts its particular pattern of remapping. If the author's model is correct, then one might hope to be able to predict with even higher accuracy the particular patterns of remapping in CA1 given sufficiently well-characterized grid field changes. This ambitious goal would require simultaneous recordings from the hippocampus and entorhinal cortex, which are beyond the scope of the current work, but would ultimately yield even more compelling evidence of the grid-to-place transformation underlying this form of remapping.

eLife Assessment

This work provides a map of enhancer-promoter interactions associated with genes controlling the development of a specific neuronal cell population. The study offers a valuable resource and integrates multiple complementary datasets to provide insights into regulatory mechanisms, although the conceptual advances are moderate and the central message could be clearer. The evidence supporting the conclusions is generally solid, but the lack of direct functional testing of key regulatory elements limits the strength of some claims.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

This study by Riegman & George et al. investigates the roles of the chromatin remodeling factor CHD7 and the proneural transcription factor Atoh1 at enhancers in cerebellar granule cells (GCs). Enhancers were categorized based on epigenetic marks and cross-referenced with promoter capture-HiC, ATAC-seq, and expression datasets to identify their long-range target genes, which were found to be enriched for critical neurodevelopmental processes. Differential expression and chromatin accessibility analyses in CHD7 knockout (KO) conditions suggest that this factor regulates a significant number of enhancers. These same enhancers are enriched for proneural transcription factor motifs, with Atoh1 being the most frequently present and likely the most affected. Finally, the direct interaction between CHD7 and Atoh1 was assessed via co-immunoprecipitation in co-transfected cells.

While the paper presents an interesting aspect of enhancer regulation in neurodevelopment, several points warrant attention:

Major Strengths:

The use of chromatin marks increases the resolution of promoter-interacting enhancer regions when integrated with capture-HiC, refining the identification of distal enhancers. Additionally, performing promoter capture-HiC experiments for the first time in this cell type constitutes a valuable resource for the community working on 3D genome organization and neurodevelopment.

Major Weaknesses:

As noted by the authors, limited sequencing depth reduces confidence in the conclusions and may result in missed weaker long-range interactions. Furthermore, the absence of capture-HiC and Atoh1 ChIP-seq experiments in the KO condition prevents direct comparison, thereby limiting the strength of the conclusions.

Additional Consideration:

Caution should be exercised regarding the assumption that every enhancer must physically contact its target promoter. While true for many enhancers, some act in trans through eRNAs or lncRNAs without direct physical contact.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors aim to identify active, long-range regulatory interactions in cerebellar granule cell progenitors (GCps). As such, the authors perform promoter capture Hi-C to map long-range interactions for all gene promoters, using cells isolated from P7 mouse brain samples. While the resolution of these maps is limited by the relatively large fragment sizes generated from a 6-bp cutter, the authors combine these interactions with other available published datasets, including from their own previous work, (e.g. ATAC-seq and ChIP-seq) to more precisely map putative enhancers within the long-range interacting regions of captured promoters. The paper further focuses on the importance of transcription factor Atoh1 and chromatin remodeller CHD7 in regulation of these putative enhancers in GCps. The authors suggest a direct interaction between CHD7 and Atoh1 by overexpression and co-immunoprecipitation in human embryonic kidney cells.

As stated by the authors, this study represents a valuable resource for researchers interested in the identification of enhancers in GCps cells, and their linked target genes. While broadly descriptive, the study does highlight some gene loci of interest and of biological relevance. For example, through integration of previously published datasets, the study resolves which putative regulatory elements at the Reln locus may regulate its activity.

This manuscript will be of interest to researchers interested in analysing long-distance targets of as well as researchers trying to understand the precise gene regulation in cerebellar development. It may also be of interest to clinical geneticists to interpret novel putative non-coding disease mutations.

Strengths:

The strengths of this manuscript are the integrated approach to identify cell-type specific enhancers utilizing available epigenomic datasets, and leveraging 3D genome topology to directly link them to their target genes. For example for the Reln gene previously implicated in cerebellar phenotypes for CHD7 mutants. The pcHi-C dataset generated in this study provides a valuable reference for the community of enhancer-promoter pairs for a specific cell-type of interest with human disease relevance.

Weaknesses:

The limitations of the study are partially addressed in the text by the authors, including the resolution from the pcHi-C using a 6-bp cutter, the limitation of sequencing depth (more interactions may have been identified with more depth), and the limited of correlation between replicates (likely due to undersampling the library). Page 9 "some additional interactions with the nearest gene promoters might be identified in our pcHi-C dataset with deeper sequencing".

Reviewer #3 (Public review):

Summary:

In this work, Riegman et al. establish the promoter interactome of cerebellar granule cell progenitors (CGPs) and identify thousands of putative enhancers regulating key genes in this cell population. The authors isolate primary CGps cells from the mouse cerebellum and perform promoter capture Hi-C in order to reanalyse previously generated epigenomic datasets (ATAC-seq, H3K4me1/3, H3K27ac) in these cells. They identify 22'797 enhancers interacting with gene promoters. The authors then use CHD7 ChIP-seq experiments to better annotate regulatory regions linked to genes deregulated upon CHD7 loss of function. After observing that CHD7 is frequently co-bound with ATOH1, they compare the binding profiles of ATOH1 and CHD7 together with genes deregulated in loss-of-function datasets, and refine the regulatory elements associated with each of these proteins.

Strengths:

The work is well designed and carefully executed, leading to an enhancer-promoter (E-P) interaction cartography that largely surpasses the current standard in the field. The pc-HiC dataset enables a deeper analysis of previously generated datasets (ChIP-seq and loss-of-function), which clearly improves the understanding of the mechanisms underlying CGps proliferation and differentiation. Moreover, the integration of published loss-of-function datasets for CHD7 and ATOH1 is relatively novel in this type of study and helps reduce the purely descriptive nature of the work. In particular, the analysis sheds light on genes with potential functions in CGps that had not previously been identified, as well as their regulatory connections. Overall, the study is convincing and supports the conclusions presented by the authors.

Weaknesses:

(1) A substantial part of the manuscript focuses on E-P interactions in CGPs, which gives the impression that this is primarily a genome organisation study. However, in this regard the manuscript does not bring major conceptual novelties. In contrast, the biological insights related to CGPs and the identification of new candidate genes likely represent the most novel aspect of the work. The authors should clarify the central message of the manuscript and reorganise the presentation of the results accordingly.

(2) The numbers presented throughout the manuscript are sometimes confusing. For instance, the authors initially report 106'589 PIF (line 175), but later only 61'928 (line 243) when calling enhancers. The relationship between these numbers is not straightforward. More generally, simplifying the nomenclature used to describe interaction analyses would help emphasise the biological insights rather than the computational framework.

(3) ATAC-seq alone is a relatively poor predictor of enhancers. In this context, H3K27ac would provide a more accurate marker of enhancer activity. This point is particularly important because the authors' data suggest that CHD7 does not function as a pioneer factor capable of opening chromatin. Instead, this role appears to be more closely associated with ATOH1. Therefore, alterations in CHD7 are more likely to affect enhancer activity (reflected by H3K27ac) rather than chromatin accessibility itself. If the authors do not have access to H3K27ac ChIP-seq data, this limitation should be explicitly acknowledged.

(4) The authors do not functionally test most enhancers and instead discuss primarily putative enhancers (with the exception of VISTA-tested elements). Although the term "putative enhancer" appears in some subsections, it is not consistently applied throughout the manuscript. This limitation should be clearly stated early in the manuscript with a sentence such as: "As these regions have not been functionally validated, they should be considered putative enhancers. However, for simplicity, we will refer to them as enhancers throughout the manuscript."

(5) Where feasible, the enhancer identified at the Reln gene should be functionally tested to demonstrate the added value of the approach.

Author response:

General Statements

We thank the reviewers for their careful and supportive reviews of our manuscript. We have addresses all the reviewers comments and extensively revised the manuscript accordingly.

During our revisions, we discovered a bug in the code that calculated the linear genomic distance between the captured promoter regions (bait regions) and the promoter-interacting fragments (PIFs). The error inadvertently halved the distance measurements in the output tables. This has been corrected in the revised manuscript and has resulted in updates to Figure 1B and corrected values in the ‘interaction_distance’ and/or ‘interaction_type’ columns of Supplementary Tables 2, 3, 6 and 8. We thank the reviewers for the opportunity to correct this.

Point-by-point description of the revisions

Reviewer #1 (Evidence, reproducibility and clarity):

In this article, the authors conducted promoter-capture HiC experiments (pcHiC) in Mouse Cerebellar granule cell progenitors (GCps) and obtained a good set of 3D genome interactions map of protein-coding genes' promoters. This dataset was later integrated with ATAC-seq and ChIP-seq experiments to identify putative enhancer regions within promoter-interacting regions, and with higher base-pair resolution than what is obtained by pcHiC experiments. This set of enhancers is then compared to and presented as being more reliable than those present in VISTA enhancer database. In addition, ATAC-seq sites and RNA-seq datasets, both obtained in WT and CHD7 and KO conditions, are integrated to correlate expression of a set of genes to the chromatin accessibility of their distal enhancer(s) which is believed to be promoted by CHD7. The study is completed by focusing on transcription factor motif analysis on CHD7-regulated enhancers which shows an enrichment for proneural transcription factors, with special emphasis on Atoh1 found to be frequently co-recruited with CHD7. Data and methods are well detailed and correctly replicated and will be useful as a resource for the community. The overlap obtained between pcHiC experiments and auto-criticized by the authors is very common and expected in this kind of experiments. In general, the conclusions drawn the article are convincing but some aspects such as comparison to VISTA and the naming of 'enhancers' should be moderated.

We thank the reviewer for their positive and constructive comments. We have amended the manuscript as indicated in detail below.

(1) The comparison of pcHiC-identified enhancers vs. VISTA enhancers should be more balanced, as the two approaches have important conceptual differences. Although VISTA enhancers are based on functional annotation, their target genes might not necessarily be correctly assigned based on the distance. On the other hand, putative enhancer regions identified by pcHiC experiments do not rely on functional testing. So both type of information are useful but can be put in perspective.

We thank the reviewer for making this point. We have amended the text to present a more balanced view e.g. “Using VISTA-designated hindbrain enhancers as an example, we identify the genes most likely regulated directly by these enhancers and update their annotation accordingly.”

(2) To increase the strength of the paper, it would be preferable that authors include simple functional enhancer assays (e.g. CRISPR deletion of contacting enhancer, luciferase assay) to support their perspective since 3D conformation information in KO condition is lacking in the article. Although ideally these experiments should be better performed for a full demonstration, it would be acceptable to at least include a simple functional assay in the WT context to demonstrate that the regulatory regions obtained by crossing genomic data are real enhancers. This point is even more critical knowing that enhancers lacking classical histone marks (H3K27ac+H3K4me1) has been described. The same comment applies to promoter interacting fragments lacking these marks, that could be missing enhancers (i.e enhancers without these marks).

To address this point, we performed luciferase assays to show that putative enhancers identified with our integrated bioinformatic approach (pcHi-C + ATACseq + H3K4me1 + H3K27ac) do indeed exhibit enhancer activity. For these experiments, we tested these putative fragments in an immortalized cell line SHH-NPD, a GCp-derived cell line generated by Fults laboratory (Jenkins et al. 2014). The results of these experiments are included as Suppl. Fig. 1 in the revised manuscript.

Minor point

- Figure 5B is lacking labels.

We apologise for this oversight – labels have now been added.

Reviewer #1 (Significance):

This article, when completed with possible revision, will be be useful for the community in terms of useful resource of experimentally determined putative enhancers in Cerebellar granule cell progenitors. It also provides some insights into the association of CHD7 and Atoh1 in distal regulation in these cells.

We thank the reviewer for acknowledging the significance of our work.

Reviewer #2 (Evidence, reproducibility and clarity):

In this manuscript, the authors aim to identify active, long-range regulatory interactions in cerebellar granule cell progenitors (GCps). As such, the authors perform promoter capture Hi-C to map long-range interactions for all gene promoters, using cells isolated from P7 mouse brain samples. While the resolution of these maps is limited by the relatively large fragment sizes generated from a 6-bp cutter, the authors combine these interactions with other available published datasets, including from their own previous work, (e.g. ATAC-seq and ChIP-seq) to more precisely map putative enhancers within the long-range interacting regions of captured promoters. The paper further focuses on the importance of transcription factor Atoh1 and chromatin remodeler CHD7 in regulation of these putative enhancers in GCps. The authors suggest a direct interaction between CHD7 and Atoh1 by overexpression and co-immunoprecipitation in human embryonic kidney cells.

As stated by the authors, this study represents a valuable resource for researchers interested in the identification of enhancers in GCps cells, and their linked target genes. While broadly descriptive, the study does highlight some gene loci of interest and of biological relevance. For example, through integration of previously published datasets, the study resolves which putative regulatory elements at the Reln locus may regulate its activity.

We thank the reviewer for their supportive comments.

We provide a summary of our major and minor comments here.

Major comments:

(1) The main take-home messages of the manuscript could be more clearly stated in the introduction to help readers understand the main conclusions of the work.

We have added a sentence to the Introduction to clarify the key take-home messages:

“We report putative distal regulatory elements for >12,000 genes, identify CHD7- and Atoh1-regulated enhancer elements and show that these factors interact and likely co-regulate the expression of key genes in the GCp lineage.”

(2) In the discussion, a previous Hi-C dataset is referred to "Reddy et al. annotated 5,175 promoter-enhancer interactions in GCps using Hi-C without enrichment (Reddy, Majidi et al. 2021)." It would be beneficial to compare the interactions identified previously with the current study (5,175 vs 46,428 interactions).

To address this comment we have performed an additional analysis and include text and Suppl. Figure 3 and Suppl. Table 13 to demonstrate the extent the two datasets compare, overlap and diverge. We have also added additional text to the discussion to highlight the difference and technical considerations between the two approaches and how they complement each other.

The 5,174 enhancer-promoter (E-P) interactions identified by Reddy et al were downloaded and intersected with the 46,428 promoter-accessible PIF regions identified in our study. The new supplementary Figure 3A illustrates that 82% (843/1207) of genes that Reddy et al identifies long-range interacting regions for are represented in our pcHiC dataset. Our pcHiC data contains information on distal interacting regions and potential enhancer regions for an additional 11,511 protein coding genes. Suppl. Figure 3B provides an overview of the Reddy et al E-P interactions that are, and are not identified in the pcHiC. We replicate 38% of Reddy et al’s E-P findings, whilst 53% of the 3229 interactions unique to the Reddy data would not be detected in the pCHiC data due to technical reasons resulting from the capture design and analysis protocol. Of the remaining interactions that are specific to the Reddy data, we identify other distal regions interacting with those same promoters . Suppl. Table 13 details the full comparision of Reddy’s E-P interactions that are found within our dataset.

The differences between the two datasets and the increased number of interactions detected in the pcHiC dataset likely result from the increased enrichment for the captured promoters enabling the detection of interactions that would have been below the detection threshold for the HiC study. In addition there are notable differences in analysis strategies for the two datasets which also contribute to differences in detection of regions. Reddy et al binned the HiC data into 10Kb regions to identify interacting regions and subsequently used chromatin marks to identify possible enhancer and promoter regions within these large regions. In contrast we have used the pCHiC and CHiCAGO algorithm to identify individual HindIII restriction fragments that are proximal to targeted promoter regions (PIFs), and prioritised those that have accessible regions within them which could represent various types of regions that play regulatory roles such as enhancers, CTCF site or facilitator regions, independent of their chromatin mark composition rather than focusing solely on enhancers.

(3) The authors identify an overlap with some of their identified enhancers with those from VISTA. Is this a fair comparison seeing as the enhancer reporters were tested during early embryonic development (e.g. E11.5 and E13.5) and seen to be active in the hindbrain, would these stages be relevant to GCps from P7? Can the authors identify ATAC-seq for example from hindbrain from embryonic stages and determine if the enhancer accessibility profile looks similar to that for the P7 GCps cells?

We thank the reviewer for this important question regarding the developmental relevance of our VISTA comparison and acknowledge that direct comparison between the time point requires careful consideration. Firstly ,to address the question of how similar the chromatin accessibility profiles are between the embryonic and P7 timepoints, we compared the ATAC-seq data from our paper to ENCODE data from the hindbrain. Of the 140 vista enhancers that were intersected with the pCHi-C dataset, 119 were identified from the lacZ studies as active in the hindbrain at E11.5 whilst 21 were identified as active at timepoint E12.5. We compared ENCODE ATAC-seq peaks from the E11.5 (ENCFF743IYX) and E12.5 ( ENCFF198TLF) hindbrain to the GCps from P7 across both the entire genome (global accessibility) as well as specifically +/- 3MB around the VISTA enhancer regions in the PIFs from the pCHiC to assess the conservation of local accessibility profiles.

When looking at the global accessibility profile of embryonic hindbrain versus P7 GCps across the whole genome there was a large degree of overlap with ~85% (E11.5) and ~88% (E12.5) of all ENCODE ATAC peaks overlapping with accessible ATAC summit regions from P7 GCps:

Author response image 1.

To identify if this was consistent in the immediate chromatin environment of the VISTA enhancers themselves, we compared the accessibility profiles across timepoints in the local environment surrounding the VISTA enhancers. This local environment was defined as a region that added an additional 3MB on either side of all VISTA enhancer positions found in PIFs. 3MB was chosen as the longest interaction found for a single VISTA element was approximately 2.7MB. Consistent with the global analysis a similarly high level of overlap of accessible regions between the timepoints was found for the local chromatin environment in surrounding the VISTA enhancers that were found within PIFs in the pCHiC dataset with ~87% (E11.5) and ~89% (E12.5) of encode detected peaks overlapping with accessible ATAC summit regions from P7 GCps.

Author response image 2.

Regions +/-3MB of VISTA enhancers in PIFs

Author response image 3.

Regions +/-3MB of VISTA enhancers in PIFs

Genome browser shots at the three example VISTA loci from Figure 1 further support this approach. In addition to this we also note that a recent study by Chen et al (2024 https://www.nature.com/articles/s41588-024-01681-2) where capture-HiC performed at E11.5 of 935 VISTA enhancers across multiple tissues confirmed that the majority of VISTA enhancer regions (61%) bypass adjacent genes which is consistent with our nearest gene comparison.

(4) The co-IP experiment appears to support the conclusion that Atoh1 and CHD7 can interact, however there are bands in lanes where there should not be (i.e. Input lanes 1 and 4 for FLAG blot). It would be recommended to repeat this result at least once. [Expected time 2-4 weeks].

This experiment has been repeated 3 times with the same result. It is normal for non-specific background bands to appear on Western blot from total cell lysates (inputs) as most antibodies have significant cross-reactivity. The anti-FLAG antibody clearly detects bands above background in lysates where FLAG-tagged CHD7 is expressed. Most critically, despite the presence of non-specific bands in input, FLAG-tagged CHD7 is only detected in immunoprecipitated samples where either FLAG-tagged proteins have been precipitated and FLAG-tagged CHD7 is expressed and HA-tagged Atoh1 has been precipitated when both FLAG-tagged CHD7 and HA-tagged Atoh1 are expressed.

(5) The methods section describes analysis of several datasets, however we could not access the code at the time of review. Do the authors intend to make this code available at the time of publication?

Yes once the publication is approved all code will be made available along with conda environment yaml files to replicate the software environment in which the analysis was performed.

(6) Page 7 "replicate one and two, respectively". Can the authors clarify the number of biological replicates performed for pcHi-C?

Two biological replicates were performed for pcHiC which were then bioinformatically combined into a ‘superset’ for CHiCAGO interaction calling as is standard practice for pcHiC data (see e.g. Cairns et al, 2016. We have revised the text to make this clearer.

Minor comments:

(1) Page 3 "controlling the expression of 577 genes in GCps" - the authors do not provide evidence that these enhancers control gene expression directly, this should be reworded.

Thank you. We have reworded to: “contacting the promoters of 577 genes” to indicate that these were identified using pcHi-C and not functional assays.

(2) Page 5 "where transient amplifying divisions exponentially expand GCps" - at what stages of embryonic/postnatal development are GCps first detected, and when do they amplify and then differentiate?

GCps that form the EGL are specified in the rhombic lip from E13.5 (Machold, 2005 and Wang, 2005) and a clear EGL can be observed in the cerebellar anlage from E14 (Ben-Arie, 1997) of development. They amplify from this stage and differentiation, induced by neurogenic factors like NeuroD1 is visible from P0 onwards (Miyata, 1999). We have amended the text to include this additional information: “GCps that form the EGL are specified in the rhombic lip from E13.5 (Ben-Arie et al, 1997; Machold & Fishell, 2005) and a clear EGL can be observed in the cerebellar anlage from E14 (Ben-Arie et al., 1997) of development. They amplify from this stage and differentiation, induced by neurogenic factors like NeuroD1 is visible from P0 onwards (Miyata et al, 1999).”

(3) Page 7 "identified 164,387 unique and significant interactions" - how is an interaction defined, a single read, or evidenced by a certain number of reads. "promoter interacting fragments or PIFs" - is PIF referring to a single read evidencing an interaction?

An interaction is defined by the CHiCAGO algorithm. The number of reads needed to score an interaction depends on the both the distance away that PIF is from the promoter (this is modelled using a distance-dependent component that accounts for decay of contact frequence with genomic distance) and also includes a component that models how the sequence or other technical artifacts might influence the capture bias of some sequences compared to others. For each promoter a background model is generated of the expected number of reads that would be captured based on the above considerations and if the number of reads for those regions exceeds this background model by a certain threshold the interaction is deemed significant using a p-value like score. In practice this means that regions further from the promoter will often require less reads to signify a significant interaction compared to regions that are much closer to the promoter. The significant PIFs in the dataset are all evidenced by a minimum of 3 reads in at least one biological replicate. We have included a short explanation of this in the methods of the revised manuscript for clarity.

The maximum reads in a single replicate library for a specific PIF was 1557, and the median number of reads per PIF was 17.

(4) Page 8. What is the distinct between PIFs and "promoter interacting regions (PIRs)"? These could be better defined in the text.

Thank you for picking up this discrepancy, we were using PIR and PIF interchany. We have amended the manuscript to refer to PIFs consistently throughout.

(5) Figure 1C-F. Labels "Random" and "PIFs" don't line up well with the two bars.

Thank you, this has been corrected.

(6) Page 9. Could the authors show some representative images for the "VISTA hindbrain enhancers" (e.g. for Figure 1I-K).

We have inserted representative images showing in vivo activity of these enhancers in mouse embryos from the VISTA enhancer site.

(7) Fig 2G, Page 11 "The 12,354 genes that were linked to a PIF containing an ATAC-seq peak were found to have a higher median expression level than the 2,049 genes that had PIFs that did not coincide with ATAC-seq peaks" - is this significant?<br />

Apologies for this oversight. We have performed a two-sided t-test on the log transformed TPMs between the two groups and have included the significance in the revised figure (p=1.8 e-40).

(8) "Gene Ontology analysis of genes with accessible PIFs revealed a significant enrichment for 119 biological processes" - can you include the GO terms in a supplementary table? Is there a way to prioritise down the 12,354 genes to a shorter more significant list of genes, this seems a long list to include in GO analysis.

We have included a supplementary table with this data in the revised manuscript (Suppl. Table 6). We included all 12,354 genes in this analysis as the point of this analysis was to demonstrate that developmental processes are enriched in the PIFs with accessible chromatin, compared to the genes where only PIFs without ATAC were identified.

(9) Page 11 - "The chromatin remodelling factor CHD7 is essential for normal expansion of GCps in the postnatal mouse cerebellum (Whittaker et al., 2017b) and deletion of Chd7 from GCps results in striking cerebellar hypoplasia and polymicrogyria (Feng et al., 2017; Reddy et al., 2021; Whittaker et al., 2017b). CHD7 haploinsufficiency is also sufficient to cause cerebellar hypoplasia and foliation defects both in mouse models and in the context of CHARGE syndrome in humans (Whittaker et al, 2017a; Yu et al, 2013)." - this appears more suitable for the introduction.

Thank you, we have moved this text to the Introduction.

(10) Page 12 "the majority of which (4,663/5,369) displayed decreased accessibility when Chd7 is depleted". This was difficult to understand initially - which are expected to be the direct effects? Increased or decreased accessibility? Perhaps it would be better to focus only on the decreased accessibility sites?

We have previously shown that the majority of differentially accessible regions in Chd7-deficient GCps show decreased accessibility. Chromatin remodelling by CHD7 could conceptually reduce or increase accessibility of a particular locus and the only way to infer direct effects are by identifying regions to which CHD7 is recruited.

Approximately ~9% of the sites that decreased in accessibility overlapped with regions bound by CHD7 (464/4663), whilst ~2% of sites that increased in accessibility overlapped with regions of CHD7 binding (14/706). Whilst it is likely that the majority of directly regulated sites decrease in chromatin accessibility when CHD7 is removed, the number of sites that increases in accessibility is small but observed and should be included for completeness.

(11) The analysis in Fig 3A reveals that only a small number of CHD7-bound enhancers show differential accessibility and altered linked gene expression upon CHD7-knock down. This requires a little more discussion - why do so many sites change in accessibility compared to the number of sites which change accessibility or are associated with gene expression change?

Identifying CHD7-regulated enhancers is challenging, mostly due to the inefficiency of CHD7 ChIP-seq. The low quality of available CHD7 ChIP-seq data has made it particularly difficult to identify CHD7 peaks. However, the integration of this data with ATAC-seq accessibility, chromatin modification and pcHi-C data has allowed us to identify a subset of enhancers that are most likely directly regulated by CHD7. However, given these technical limitations, we would be hesitant to conclude from the present data that the majority of chromatin accessibility changes in enhancers in Chd7-deficient GCps are indirect. We have added the following text to the discussion to indicate this: “Identifying CHD7-regulated enhancers is challenging, mostly due to the inefficiency of CHD7 ChIP-seq. The low quality of available CHD7 ChIP-seq data has made it particularly difficult to identify CHD7 peaks. However, integrating CHD7 ChIP-seq data with ATAC-seq accessibility, histone modification ChIP-seq and pcHi-C data has allowed us to identify a subset of enhancers that are most likely directly regulated by CHD7. However, given these technical limitations, we would be hesitant to conclude from the present data that the majority of chromatin accessibility changes in enhancers in Chd7-deficient GCps are indirect, as suggested by the data in Fig. 3A.”

(12) Page 12 - "Over-representation analysis confirmed an enrichment of genes linked to nervous system development" - could this and the GO term analysis be included in a supplementary figure?

We have included these results as Suppl. Table 7 in the revised manuscript.

(13) Fig 3D - what does the arrow represent in the chromatin schematic?

The arrow in the schematic indicates chromatin remodelling – we have clarified this in the figure legend and added headings to these panels to indicate the 3 different types of elements: Direct CHD7 targets, Indirect targets and CHD7-bound elements.

(14) Fig 3G does not appear to be referenced in the text. The value of the Upset plots in the main figure 3 wasn't very clear, perhaps these could be moved to the supplement? Is there a clearer plot to support the conclusion "CHD7 primarily regulates enhancers".

We apologise, the panels were mis-labeled in the text. This has now been corrected. We hope that the amendments in response to point 13 above now clarifies these findings showing that direct CHD7 targets are characterised by active enhancer marks.

(15) Page 14 "putative consensus sites for proneural bHLH TAL-family of proteins Neurog2, Neurod2, Neurod1, and, Atoh1 in elements" - HOCOMOCO motifs are only shown for Atoh1 and Nhlh1. It may be valuable to show the sites for all the listed TFs. What does white represent in the heatmap in Fig 3H? This plot is difficult to interpret, and also relatively small in the figure but appears important to conclusions. Perhaps Fig 3H could be made more prominent?

Thank you for highlighting that the white boxes might be confusing. The white blocks indicate that these motifs do not pass threshold for significantly enriched in the dataset based on the p and q values.This has now been clarified in the figure legend.

We have enlarged panel H to make more prominent.

(16) Page 15 - "Myb was the only motif specific to CHD7 bound regions that changed in accessibility compared to those that exhibited accessibility changes without CHD7 binding or CHD7 binding without accessibility changes (Suppl. Fig. 1)." I couldn't interpret this sentence, requires clarifying.

We agree that this description is confusing and since it is difficult to draw clear conclusions about the significance of enhancers with Myb motifs in this context, we have removed this sentence from the revised manuscript.

(17) Page 16 and Fig 4B - a discussion of why both up and down regulated genes are detected for Atoh1 depletion? Which class of genes are expected to be directly regulated (the down-regulated genes)?

Like most transcription factors, ATOH1 may be able to function as both a repressor and activator depending on the context. Although the majority of genes are downregulated in Atoh1-defivcient cells, suggesting that Atoh1 functions as an activator in most cases, our analysis have identified several up-regulated genes that contain Atoh1 ChIP-seq peaks in their cognate enhancers (See Suppl. Table 7), consistent with these also being direct Atoh1 targets.

(18) Fig 5B - the genomic traces are not labelled in this figure.

Thank you, labels have been added.

(19) Page 17 - "Pathway enrichment analysis of the 22 genes compared to all genes that were expressed in GCps shows a significant enrichment of terms: Hypoplasia of the pons (HP:0012110 P=0.006) and Abnormal pons morphology (HP:0007361 P=0.016) from human phenotype ontology, due to the presence of Reln, Dcc, Mab21l1 and Gli2." - this analysis should be included in the supplementary tables.

These results have been included as Suppl. Table 12 in the revised manuscript.

(20) Do the authors have a suggestion for which domains of Atoh1 and CHD7 could be interacting? Could the authors design truncated constructs for overexpression in HEK cells to test this hypothesis? [Expected time 4-6 weeks, interesting but not essential to do experimental work here].

We agree this is an interesting question. Our collaborator, Professor Peter Scambler (UCL) has performed a yeast two hybrid screen for CHD7 interacting proteins in a mouse E11.5 library using the CHD7 BRK domain (aa 2521-2708) as bait. The screen had a single hit, which encompassed the N-term 127aa of ATOH1 (personal communication). This observation supports our co-IP data and suggests that the N-terminus of ATOH1 interacts with the BRK domain of CHD7 but further validation will be needed to confirm this.

(21) Page 28 "Differential accessibility analysis was performed using DESeq2 (v 1.22.1)" and Page 19 "Whereas chromatin accessibility at some of these enhancers were affected by Chd7-deficiency" - what were the cutoffs used for looking at differentially accessible regions? Complete loss of accessibility or a quantitative change?

Quantitative change rather than complete loss was used. Thresholds based on adjusted p-values (padj<0.05) were used as indicated in the methods.

Requested comments on referencing:

- "Long-range" - how do the authors define long-range? Can this be referenced. CO? good reference here.- look to CHiCAGO paper

- "When chromatin conformation or 3D organisation data is not available, studies typically assign regulatory elements to the nearest gene promoter" - needs referencing.

- "Many of these 22 genes regulated by CHD7 and Atoh1 have established critical roles in cerebellar development, including Neurod2, Pax6 and Gli2 (Fig. 5B)" - needs referencing. "from human phenotype ontology, due to the presence of Reln, Dcc, Mab21l1 and Gli2" - needs referencing.

Thank you, references have been added.

- "active enhancers (H3K27ac+, H3K4me1+), promoters (H3K27ac+, H3K4me3+), regulatory elements (H3K27ac+, H3K4me1+, H3K4me3+), or poised enhancers (H3K4me1+)" - needs referencing.

Thank you, references have been added.

- Reference required in main text for VISTA (e.g. Visel et al., 2007)

Thank you, reference added.

Reviewer #2 (Significance):

The strengths of this manuscript are the integrated approach to identify cell-type specific enhancers utilizing available epigenomic datasets, and leveraging 3D genome topology to directly link them to their target genes. For example for the Reln gene previously implicated in cerebellar phenotypes for CHD7 mutants. The pcHi-C dataset generated in this study provides a valuable reference for the community of enhancer-promoter pairs for a specific cell-type of interest with human disease relevance.

We thank the reviewer for recognising the potential value of our work to the community.

The limitations of the study are partially addressed in the text by the authors, including the resolution from the pcHi-C using a 6-bp cutter, the limitation of sequencing depth (more interactions may have been identified with more depth), and the limitated of correlation between replicates (likely due to undersampling the library). Page 9 "some additional interactions with the nearest gene promoters might be identified in our pcHi-C dataset with deeper sequencing".

We thank the reviewer for highlighting our acknowledgements of the potential limitations of our work.

Additional limitations include the use of the VISTA browser mouse LacZ embryos to validate some of their enhancers, the limitation here being that the VISTA browser tests enhancers at embryonic stages (focused at E11.5 and E13.5) while the GCps cells were collected at P7. The LacZ images from VISTA are also not shown. The HEK cells used for the co-IP could be seen as a limitation as these are not relevant cells for the cell state studied, the authors could clarify their use of these cells.

We thank the reviewer for their careful assessment of the limitations of our study. We have now included images of the VISTA enhancers in Fig. 1I,J,K. Rather than a limitation, using irrelevant cells for co-IP might be seen as a better approach, as conceivably the chances of an indirect interaction between the two proteins being tested by a bridging complex is less in an irrelevant cell types that might not contain such complexes. Either way, HEK293T cells is the standard laboratory model for co-IP studies as they can be transfected with ease.

The study reported here is largely based on previous work from the authors (Whittaker et al 2017b). This study reported that the chromatin remodelling factor CHD7 is essential for normal expansion of GCps in the postnatal mouse cerebellum and deletion of CHD7 from GCps resulted in the phenotype of cerebellar hypoplasia. This study also largely leverages previously published datasets from the Whittaker et al 2017b (e.g. CHD7 deletion data) and reanalyses it in the light of the new pcHi-C datasets.

This manuscript will be of interest to researchers interested in analysing long-distance targets of as well as researchers trying to understand the precise gene regulation in cerebellar development. It may also be of interest to clinical geneticists to interpret novel putative non-coding disease mutations.

We thank the reviewer for highlighting the wide interest of our manuscript.

In assessing this manuscript, my expertise lies in models of human development and gene regulation, with a focus on enhancer function.

Reviewer #3 (Evidence, reproducibility and clarity):

Riegman et al have explored the gene regulatory landscapes of cerebellar granule cell progenitors (GCps). They have generated promoter capture Hi-C data to identify regions that interact with promoters in these cells. In addition they generate ATACseq data in wild-type and CDH7 knock-out cells. They integrate these data to identify enhancers that potentially regulate genes in GCps. In addition, the authors identify an interaction between CHD7 and ATOH1, whose binding sites also overlap in the genome.

The dataset can be potentially interesting for people studying cerebellar development.

I have a few concerns regarding the paper. The most pressing one is that the authors seem to equate interactions in pcHi-C with regulation. This is problematic for two reasons. First whether interaction equates regulation is still debated and whether this can be detected with a low-resolution C-method (i.e. using HindIII) is a further point of contention.

We thank the reviewer for pointing this out. We agree and apologise for not being clear in our manuscript. We have made the necessary amendments to indicate that pcHi-C by itself only assess proximity in the nucleus, not function.

We acknowledge the limitations of the pcHi-C method, including that resolution is limited by the use of a restriction enzyme. However, we (see e..g. Suppl. Fig. 1) and others (see e.g. Freire-Pritchett et al (2017) and Mifsud et al (2015)) have used this approach successfully to identify functional enhancer elements.

The second issue has to do with the way the pcHi-C data is interpreted. What is detected as a significant interaction by Chicago are regions that have a contact frequence above background. This means that local regions with a (much) higher contact frequency may not be called as significant. When we follow the logic that contact frequency is related to gene activation (which may not necessarily be true) whether a fragment is more frequently contacted than the background should not matter (relative contact frequency), rather it should be interpreted based on the absolute contact frequency.

The reviewer is right that local regions will have a higher contact frequency and that local contacts aren’t always captured by the CHiCAGO model. However, the purpose of this study was to prioritise the identification of distal elements that are not captured by existing methods including nearest gene annotation.

There are a number of reasons why absolute contact frequency might not be an appropriate measure to infer gene regulation: 1) Many factors can affect the absolute contact frequency including the proportion of cells that are exhibiting active transcription at that time across a population, especially if expression is limited to a small number of this population at that time. 2) Absolute contact frequency assumes that more contact results in more regulation which is not necessarily true and would depend on the combination of factors that are associated with that regulatory element. Figure 1 from https://www.nature.com/articles/s41596-023-00817-8 - Figure 1 – Micro capture C show that regions with low absolute contact frequency compared to adjacent regions have potential to regulate gene expression, as have other studies that have used CHiCAGO to identify regulatory elements. 3) The sequence of some fragments makes them more likely to captured or enriched in the HiC protocol, which the relative contact frequency above background controls for.

This becomes relevant because the authors claim that 80% of enhancers are wrongly annotated based on their metrics. The only way to correctly annotate an enhancer is to knock it out and checking the effect on genes in the vicinity. Therefore, to claim that their method can correctly annotate enhancer is grossly overstated, particularly when considering the issues with contact frequency stated above. Therefore, claims like 80% of enhancers are wrongly annotated should be removed from the paper. The authors should discuss how to annotate enhancers, in the Discussion and what the proper method is for annotations.

We have amended the text to indicate that we do not suggest that VISTA enhancers are wrongly annotated but incompletely assigned. We apologise for making this suggestion in the first draft. There is however complementary evidence from Cheng et al (2024), now referenced in the revised manuscript, that also find 60% of the VISTA enhancers skip their adjacent gene. It is also well established in the literature that nearest genes are not always regulated.

Other points:

- The authors claims that PIFs have 2.14 and 2.69 fold enrichment of H3K4me1 and H3K27ac sites. Did the authors use the whole genome as background. If so, they should take into account that promoter are more likely in regions of high gene density, which are more dense in active marks. It would be better to perform local, circular permuation of the the PIFs around the promoter.

The reviewer is correct that a whole genome background is not an appropriate background for testing enrichment of active marks within PIFs. Fortunately, this is taken into account in the CHiCAGO enrichment test which selects the background from fragments that are matched to the same distance of the PIFs to account for the observation that promoters are more likely in regions of high gene density and are therefore more enriched for active chromatin modifications.

- The authors talk about "lead PIF", which is the fragment with the "most significant CHICAGO score". What does this mean? Something is significant or not, despite common misuse of the term there is no gradient of significance.

The reviewer makes a good point here and we apologise for the oversight in wording and have corrected the text to be more specific that the lead PIF is the one with the highest ChiCAGO score.

- In the GO analysis the categories with the lowest p-value are presented, but this biases for large categories. It would be more relevant to also select for and show the enrichment scores.

We agree with the reviewer that a drawback of GO analysis is that it biases for large categories and that if by ‘enrichment score’ the reviewer means the –log10(p-value) we have included that in the supplementary tables which also includes the size of the category and number of genes detected in it.

Reviewer #3 (Significance):

The study provides a dataset that may be interesting for people studying cerebellar development. In that sense the data is mostly interesting from a fundamental viewpoint. The data seem of good quality.

The authors claim that they a very sizeable fraction of enhancers are misannotated, but I do not believe that this is correct.

We thank the reviewer for pointing this out. We apologise for creating the impression that VISTA enhancers are incorrectly annotated. We have amended the text to reflect that these are incompletely annotated.

My expertise is 3D genome, bioinformatics.

eLife Assessment

This important study concerns the propagation of waves in bacterial biofilms, bridging active matter physics and bacterial biophysics. The experimental observations are solid, and the theoretical interpretation and model validation have been refined with revisions. This work will be of interest to microbiologists, biophysicists, and researchers studying collective behavior in biological systems.

Reviewer #1 (Public review):

Summary:

Overall, this is an interesting paper. The authors identify several experimental knobs that can perturb mechanical wave behavior driven by pili feedback. They frame these effects in terms of nonreciprocal interactions. While nonreciprocity could indeed play a role, it raises the question of whether mechanical feedback might also contribute. Phenomenological models can be useful, but the model currently lack direct mechanistic insight. It would be more compelling to formulate the model around potential mechanochemical feedback, which could help clarify the underlying microscopic mechanisms.

Strengths:

Report of mechanical waves in bacterial collectives, mechanism has potential application in multicellular context such as morphogenesis.

Weaknesses:

A minor concern about the language of 'left-right asymmetry.' I believe the correct term is simply 'radial asymmetry' which is a distinct concept. Left-right is not well defined in the current context.

Reviewer #3 (Public review):

Summary:

The revised manuscript presents a compelling study of radially propagating metachronal waves on the surface of Pseudomonas nitroreducens biofilms, combining experiments with two theoretical descriptions (a local phase-oscillator model and an active solid/active gel model). The central experimental findings-spiral/target/planar wave patterns, their controllability via water/PEG/temperature perturbations, and the correlation between frequency gradients and propagation direction-remain highly interesting and relevant to both bacterial biophysics and active-matter physics. The revised manuscript also adds substantial new material, including additional analyses of defect dynamics and clearer discussion of the relationship between the two models. The study continues to have a strong interdisciplinary appeal and the potential to stimulate further work on collective oscillations in biological active media.

Strengths:

The authors have substantially addressed the major conceptual issue raised in the previous round by clearly distinguishing between nonreciprocity and frequency gradients / global asymmetry. This clarification significantly improves the theoretical interpretation and resolves an important source of confusion in the original version.

The revised manuscript also improves the connection between the phase-oscillator and active-solid descriptions. In particular, the authors now explain more explicitly how the phase variable is defined in the reduced oscillatory dynamics of confined biofilm motion, and they state that they added a schematic illustration and simulation details (including parameter values and the elastic-force definition) to improve reproducibility. This directly addresses one of my previous major concerns.

A notable improvement is the newly added defect-based analysis of waveform transitions (spiral -> target -> planar). The revised text argues that defect motility is a key control parameter, linked experimentally to moisture-dependent elasticity and theoretically to nonreciprocity / defect-pair stability. This provides a more concrete mechanistic bridge between experimental perturbations and the modeling framework than in the previous version.

The manuscript now gives a clearer experimental-theoretical narrative for how environmental manipulations (drying, water addition, PEG, heating) affect wave patterns through changes in effective elasticity and activity, including a useful distinction between short-timescale and long-timescale temperature effects. This added discussion strengthens the biological interpretation and makes the modeling assumptions easier to follow.

Weaknesses:

The main remaining limitation is the level of quantitative correspondence between theory and experiment. The revised manuscript now provides a stronger qualitative/mechanistic link, but the mapping between model parameters (e.g., effective coupling terms / elasto-active parameters) and directly measurable biofilm properties is still limited. The authors acknowledge this point, and I agree that it is technically challenging in the present system. However, this means the theoretical framework is currently most convincing as an effective mechanistic model rather than a quantitatively predictive one.

Relatedly, some conclusions about parameter-level control (especially in connecting moisture/temperature manipulations to specific model parameters) remain qualitative. I do not view this as fatal, but I recommend that the manuscript clearly state this scope and avoid overstating the quantitative predictive power of the theory.

Although the terminology has improved compared with the original version, the revised manuscript still uses "left-right asymmetry" in places where the underlying geometry and symmetry are more general (e.g., radial inward propagation in circular colonies). Since this wording was one of the original points of confusion, I suggest one final pass to ensure the symmetry language is consistently precise throughout the main text and figure captions.

Author response:

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

eLife Assessment

This important study concerns the propagation of waves in bacterial biofilms, bridging active matter physics and bacterial biophysics. While the experimental observations are solid, the theoretical interpretation and model validation are currently incomplete and require further refinement. This work will be of interest to microbiologists, biophysicists, and researchers studying collective behavior in biological systems.

In the revised manuscript, we have added new experimental results that strengthen the connection between our observations and the modeling framework used to interpret the collective oscillations. We have not introduced a new theoretical model; rather, we employed established active matter models and sought to link the observed phenomena to these frameworks. In particular, our new data demonstrate that the transition between the motile and biofilm-forming states specifically modulates the elasticity and elasto active coupling of the bacterial structure. This behavior is in excellent agreement with the predictions of the active solid model. All the experimental details are given below. We believe that the revised version of the manuscript now establishes this connection more clearly and convincingly.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Overall, this is an interesting paper. The authors have found multiple experimental knobs to perturb a mechanical wave behavior driven by pilli feedback. The authors framed this as nonreciprocal interactions - while I can see how nonreciprocity could play a role - what about mechanical feedback? Phenomenological models are fine, but a lack of mechanistic understanding is a weakness. I think it will be more interesting to frame the model based on potential mechanochemical feedback to understand microscopic mechanisms. Regardless, more can be done to better constrain the model through finding knobs to explain experimental observations (in Figures 3, 4, 5, and 7).

We thank the reviewer for the positive assessment and for highlighting this important point. The reviewer is correct that the phenomenological Kuramoto-based model does not explicitly show the detailed cell–cell interactions. However, the active solid model is formulated on detailed elastic couplings and active forces, which inherently represent mechanical feedback within the biofilm structure. In this framework, nonreciprocity emerges naturally from the tensorial nature of active forces between bacteria—a concept already well established in the active matter literature. Importantly, this mechanism is purely mechanical and closely parallels nonreciprocal hydrodynamic interactions among active particles, which also arise from tensorial couplings.

In our system, elastic interactions within the biofilm matrix, combined with pilus-generated active forces, provide a natural origin for nonreciprocal interactions. To further validate this, we improved our imaging to record single-cell dynamics both at the colony edge and on the biofilm surface. (new supplementary Video). These experiments show that motile bacteria at the leading edge of the biofilm structure do not generate waves, whereas stationary bacteria within the biofilm display local oscillations within the elastic network. This observation supports the view that collective oscillations are a property of the elastic biofilm state rather than of freely motile cells.

Moreover, the main control parameter for these oscillations is the ratio between elastic strength and the active force generated by pili. In the active solid model, this ratio is captured by the parameter π and alpha terms. Experimentally, we can tune this ratio simply by adding or removing water from the biofilm, thereby modulating its elasto active coupling. We further motivated the controllability of this feature experimentally. We let the plate dry nonuniformly and observed that the transition between spiral target and plane waves could emerge spontaneously across the plate (see Figure 3a). This observation also states the importance of moisture in the biofilm. Starting from this point we established the connection between experimental observation and modelling. In our new simulations we also noticed that the transition from spiral to target wave is particularly driven by merging processes of different topological charges +/- 1 spiral pairs. This critical point was also confirmed by modelling which links the process to elasto active coupling. Further we supported our claim by imagining the edge and the biofilm structure. These new results clarify that elastic structure of the biofilm is critically important (Supplementary Figure 3). We have clarified this mechanistic link in the revised manuscript and rewritten the relevant sections to make this connection explicit.

Modification in the manuscript:

“To gain deeper insight into the mechanisms underlying wave formation, we imaged the dynamics of individual bacteria from the fingering regions toward the center of the biofilm. This distinction is critical because, unlike the biofilm center, the edges do not generate waves. We observed that bacteria near the fingering regions remain motile and exhibit collective flow. In contrast, bacteria at the biofilm center are surface-attached and undergo periodic lifting motions. This behavior strongly resembles Mexican-wave dynamics.”

“We further found that the central region of the biofilm is mechanically more elastic, whereas the edge regions—where wave formation is absent—are motile. These observations suggest that gradual biofilm maturation is a key factor that transforms motile bacteria into a periodically moving but spatially constrained state. Consistent with this picture, the PAO1 strain, which has a strong biofilm-forming capability, completely suppresses surface oscillations. In contrast, the PA14 strain exhibits intermediate behavior, sustaining a partial transition between motile and locally constrained dynamics. Remarkably, signatures of this transition and wave generation are already detectable at the earliest stages of finger formation.”

Strengths:

The report of mechanical waves in bacterial collectives. The mechanism has potential application in a multicellular context, such as morphogenesis.

We thank the reviewer for the positive assessment and for highlighting this potential broad impact of our findings.

Weaknesses:

My most serious concern is about left-right symmetry breaking. I fail to see how the data in Figure 6 shows LR symmetry breaking. All they show is in-out directionality, which is a boundary condition. LR SM means breaking of mirror symmetry - the pattern cannot be superimposed on its mirror image using only rigid body transformations (translation and rotation) - as far as I am aware, this condition is not satisfied in this pattern-forming system.

We thank the reviewer for pointing out this critical issue. We acknowledge that we overlooked the distinction between biological and physical definitions of left–right symmetry in our initial submission, and we agree that our terminology was confusing.

In developmental biology, the term “left–right symmetry breaking” is often used to describe asymmetric flows generated by nodal cilia, which subsequently establish developmental asymmetry. This usage differs fundamentally from the physical definition of mirror symmetry breaking, which refers to chirality switching upon mirror reflection. As the reviewer correctly noted, our system does not exhibit mirror symmetry breaking in this strict physical sense.

To avoid confusion, we have revised the manuscript and replaced the term left–right symmetry breaking with left–right asymmetry between the edge and the center of the biofilm. This asymmetry arises from frequency gradients across the biofilm and is not a trivial boundary effect. For circular colonies, this phenomenon is more accurately described as radial asymmetry. We have rewritten the relevant sections of the manuscript to clarify this distinction and prevent misinterpretation.

Reviewer #2 (Public review):

Summary:

This manuscript by Altin et al. examines the dynamics of bacterial assemblies, building on previously published work documenting mechanical spiral waves. The authors show that the emergent dynamics can be influenced by various factors, including the strain of bacteria and water content in the sample. While the topic of this paper would be of broad interest, and the preliminary results are certainly interesting, various aspects of this paper are underdeveloped and require further exploration.

Strengths:

One of the nice features of this system is the ability to transition between the different states based on the addition or withdrawal of water. The authors use a similar experimental model system and mathematical model to previously published work (Reference 49), but extend by showing that the behaviour can be modified through simple interventions. Specifically, the authors show that adding water droplets or drying the sample through heating can result in changes in the observed wave structure. This represents a possible way of controlling active matter.

The mathematical model proposed in this paper involves a phase-oscillator model of Kuramotostyle coupling (similar to previously reported models). A non-reciprocal phase lag is introduced in order to facilitate the patterns seen in experiments. The qualitative agreement in the behaviour is quite striking, showing both spiral waves and travelling waves.

We thank the reviewer for the positive assessment and for pointing out areas that required further development. The reviewer is correct that our work builds on previously reported bacterial spiral wave systems; however, there are several significant differences that we now emphasize more clearly in the revised manuscript.

First, our study involves a different bacterial species and reveals a distinct dynamical process: the waves we report are strictly localized on the surface of the biofilm, in contrast to the bulk oscillations detected through density fluctuations in the earlier work (Ref. 49). The surface waves in our system resemble “Mexican wave”-like motions, in which surface bacteria periodically lift upward. To highlight this key distinction, we performed new imaging experiments that directly visualize this process. (New Video 5 and 6, Author response image 1).

Second, we systematically compared different bacterial strains, including pathogenic species such as P. aeruginosa PA14 and PAO1, alongside our BSL-1 strain. This comparative approach demonstrates that the observed phenomenon spans strains with different pathogenicity levels, and genetic variations while also showing that our strain provides a safer and more broadly usable model system for laboratory investigations.

Third, the modeling frameworks differ. Whereas the referred study relied primarily on phase models similar to those used in cilia systems, we combine a delayed Kuramoto-style oscillator model with an active solid model. This combination provides both a phenomenological description and a physical interpretation of the collective dynamics. We acknowledge that, in the original submission, the physical interpretation of the model in relation to our experimental system was underdeveloped. In the revision, we have now established this link explicitly through the elasticity and elasto active coupling of the biofilm. Specifically, we show that the transition from motile to biofilm states is accompanied by changes in elasticity, which directly influence the observed transitions between different types of wave defects. This connection is consistent with prior theoretical works and has even been only studied in robotic active matter systems.

Together, these clarifications and new results reinforce the novelty of our findings and establish a stronger connection between the experiments and the modeling framework.

Author response image 1.

Comparison between the elastic biofilm core and the motile colony edge. Highresolution video recordings revealing individual bacterial motion highlight the key physical differences driving wave-generating. Time-lapse snapshots show that bacteria at the colony edge move freely and form fingering structures, whereas bacteria in the elastic central biofilm periodically lift vertically, producing a Mexican-wave–like collective motion across the surface. See new Video

Weaknesses:

The principal observation of the paper - that spiral waves emerge in these systems and can be controlled in various ways - is not linked to microscale dynamics at the cell level. It is recognised that hydrodynamics can introduce non-reciprocity, an essential ingredient of this model. However, in this work the authors have not identified a physical mechanism for the lag, e.g., either through steric interactions or hydrodynamic disturbances. This is also relevant in the phase oscillator modelling section. In low Reynolds number flows, dynamics are instantaneously determined. In this light, what does the phase lag term represent?

The reviewer is correct that, at low Reynolds numbers, fluid dynamics are instantaneous and do not generate real temporal delays. However, nonreciprocity in hydrodynamic interactions can still emerge from the tensorial structure of the Blake–Oseen Green’s function. In this formalism, the effective asymmetry can be represented mathematically as a phase-lag–like term. This has been theoretically demonstrated in Ref.40. While this is not a literal time delay, it functions analogously by breaking odd symmetry in the coupling.

In our system, strong long-range hydrodynamic interactions are absent, as the bacteria are embedded in an elastic biofilm matrix. Instead, the dominant interactions are active elastic couplings mediated by pili and biofilm structure. The elastic solid model behaves in a way that is conceptually similar to the hydrodynamic case: pili-induced deformations of the elastic medium produce anisotropic stresses that play a role analogous to the tensorial hydrodynamic Green’s function. Thus, the phase-lag term in our Kuramoto-based model can be interpreted as an effective representation of these nonreciprocal elastic interactions.

We have clarified this point in the revised manuscript by explicitly connecting the phenomenological phase-lag term to the underlying elastic coupling in biofilms.

What is the origin of the coupling term, b? Can this be varied systematically or derived from experimental measurements or parameters?

The term b represents the enhanced elasto-active coupling of the pili process. The length of the Pili varies, and the elongated Pili has more potential to modulate the coupling between bacteria which is known to depend on a critical threshold. This process resembles the pinning dynamics and is driven by the activity of molecular motors within the pili machinery. However, the detailed mechanisms that set the effective coupling strength remain highly complex and are not yet fully understood.

At present, we do not have a direct way to systematically manipulate b in experiments. A major technical limitation is the nanoscale nature of type IV pili: these protein assemblies are extremely small and difficult to monitor or manipulate directly. Even basic tools such as GFP-based labeling have proven challenging to implement, which restricts our ability to track the detailed dynamics of these structures in live biofilms.

While we cannot currently derive b directly from experimental parameters, we emphasize in the revised manuscript that b should be understood as an effective parameter capturing the excitability of pili retractions. We also highlight this limitation and note that future advances in molecular imaging and manipulation of pili will be essential for quantitatively linking b to microscopic processes.

Classification of wave properties is an important aspect of this paper, but is not accomplished in a quantitative sense. What is the method for distinguishing between travelling and spiral waves? There is a range of quantitative tools that could be used to investigate these dynamics (and also compare quantitatively with the models). For example, examining the correlation functions and order parameters could assist with the extraction of wave features (see extensive literature on oscillator models).

We thank the reviewer for emphasizing this important point. In the revised manuscript, we have incorporated the classic Kuramoto order parameter (S) to characterize the dynamics in our model simulations. However, this metric is not directly applicable to our experimental system, because we cannot resolve the phase of individual bacteria at large scales.

Instead, we have focused on a flux-based parameter, as previously used in Ref. 40, which can be measured experimentally from collective surface dynamics. Interestingly, we find that the directional flux extracted from our experimental movies closely matches the trends predicted by the model order parameter. We suspect that this similarity arises from the combination of our optical illumination method and the characteristic surface modulations of the biofilm. While we currently lack a rigorous theoretical justification for this correspondence, so we want to keep this discussion in the review document.

In summary, we now use the classic Kuramoto order parameter in simulations and rely on the experimentally accessible flux measure for our experimental data. This dual approach allows us to compare model and experiment in a consistent manner.

Author response image 2.

Critical order parameters of the coupled biofilm system. (a) The Kuramoto global order parameter increases continuously as the system becomes globally synchronized. In contrast, in the nonreciprocally coupled system the order parameter saturates at a critical level. (b) In the experimentally observed biofilm, however the flux generated by the coupled oscillations provides a more appropriate measure of synchronization. Blue curves indicate directionally propagating planar waves, red curves correspond to spiral wave formation, and green curves represent the globally synchronized reciprocal system.

Author response image 3.

Comparison of flux profiles of the simulations with experimental measurements. Directional optical illumination enhances the flux term on the surface of the biofilm.

The methodology of changing the dynamics through moisture content appears to be slightly underdeveloped, e.g., adding water involves a droplet, and removing water is accomplished by heating (which presumably could cause other effects). Could the dynamics not be controlled more directly by varying the humidity?

We thank the reviewer for this valuable suggestion. Our results indicate that water content in the biofilm plays a key role in driving the transition to the biofilm state by modulating its elasticity. During the initial submission, we did not know how to systematically vary humidity without simultaneously altering temperature. Standard approaches typically involve water evaporation in controlled chambers, which inherently changes both parameters.

Following the reviewer’s recommendation, we first measured the ambient moisture levels inside closed culture plates. To our surprise, the relative humidity was already ~98%, leaving virtually no room to increase it further. We then attempted to decrease humidity by flowing dry synthetic air, but even under these conditions we could not reduce it below ~85%, and achieving this required unrealistically high flow rates. Moreover, we noticed that in closed-lid NGM plates, evaporation is already substantial, and when the lid is left open the evaporation rate reaches ~1 µm/s. This rapid surface thinning severely limits the quality of long-term time-lapse imaging.

Taken together, these technical constraints explain why we have to reliy on localized perturbations such as water droplets and heating rather than global humidity control. We have clarified this point in the revised manuscript and now explicitly discuss both the challenges and limitations of humidity-based approaches.

At the same time, the authors also mention that temperature itself plays a role in shaping the behaviour. What is the mechanism for this? Is it just through evaporation? Since the frequency increases with temperature, could it just be that activity increases with temperature?

We thank the reviewer for raising this critical point. We believe that temperature has two distinct impacts operating on different timescales.

Short timescale (~minutes): We observed that biofilm oscillations respond to temperature changes very rapidly and in a reversible manner. This timescale is too short to be explained by modulation of water content or bulk elasticity of the biofilm. Instead, we attribute the immediate frequency increase to enhanced biological activity of the bacteria at elevated temperatures.

Long timescale (~tens of minutes to hours): During processes such as the transition from planar to spiral waves, prolonged heating can significantly alter the biofilm structure. These changes are not reversible and likely involve modifications of elasticity and other structural properties.

In the modeling framework, the short-timescale effect is represented as an increase in the active force term, while the long-timescale effect is captured by concurrent changes in both the active force and the elastic properties of the biofilm. We have clarified this mechanism and its representation in the revised manuscript.

Reviewer #3 (Public review):

Summary:

This manuscript presents a novel investigation into unidirectionally propagating waves observed on the surface of Pseudomonas nitroreducens bacterial biofilms. The authors explore how these waves, initially spiral in form, transition into combinations of spiral, target, and planar patterns. The study identifies the periodic extension-retraction cycles of type IV pili as the driving mechanism for wave propagation, which preferentially moves from the colony's edge to its center. Furthermore, the manuscript proposes two theoretical models-a phase-oscillator model and a continuum active solid model-to reproduce these phenomena, and demonstrates how external manipulations (e.g., water droplets, temperature, PEG) can control wave patterns and direction, often correlating with oscillation frequency gradients. The work aims to bridge the fields of activematter physics and bacterial biophysics by providing both experimental observations and theoretical frameworks for understanding these complex biological wave phenomena.

We thank the reviewer for the positive assessment of our work and for highlighting both the novelty and the key contributions of our study.

Strengths:

The experimental discovery of unidirectionally propagating waves on bacterial biofilms is highly intriguing and represents a significant contribution to both microbiology and active-matter physics.

The detailed observations of wave pattern transitions (spiral to target to planar) and their response to various environmental perturbations (water, temperature, PEG) provide valuable empirical data. The identification of type IV pili as the driving force offers a concrete biological mechanism. The observed correlation between frequency gradients and wave direction is a compelling finding with potential for broader implications in understanding biological pattern formation. This work has the potential to stimulate further research in the collective behavior of living systems and the physical principles underlying biological organization.

We thank the reviewer once again for emphasizing the importance of wave directionality. We also believe that this phenomenon may provide insight into early symmetry-breaking processes observed in developmental biology, where oxygen or nutrient gradients in dense environments could play a similar role.

Weaknesses:

The manuscript attempts to link unidirectional wave propagation to non-reciprocal couplings but ultimately shows that the wave direction is determined by the gradient of the oscillation frequency. The couplings in the two theoretical models are both isotropic and thus cannot dictate the wave direction. A clear distinction should be made between non-reciprocity as a source of wave generation and non-uniformity as a controlling factor of wave direction.

We greatly appreciate the reviewer’s careful evaluation, particularly for highlighting this important and often confusing distinction. The relationship between nonreciprocity, spontaneous symmetry breaking, and frequency gradients has also been a challenging concept for us and required significant effort to clarify.

Recent theoretical studies have established that traveling wave formation requires nonreciprocity, which provides a framework for understanding phenomena ranging from spiral to target and planar waves. In our system, nonreciprocity arises between the displacement field (U) and the pili force vector (P): as a result in broken phase U effectively “chases” P, breaking PT symmetry locally and thereby enabling the generation of local directional flux and traveling waves. In this sense, nonreciprocity is essential for travelling wave generation and spontaneous symmetry breaking in either direction.

However, we now agree that global directionality (always from right to left, or edge to center) is set by an independent factor—namely, the oscillation frequency gradient across the biofilm. Thus, while nonreciprocity determines whether waves can travel, frequency gradients determine the large-scale direction in which they propagate. Put differently, PT symmetry is already broken spiral waves due to nonreciprocity, but global asymmetry (frequency gradients) is required to align the overall propagation in one direction.

We have clarified this distinction in the revised manuscript, emphasizing that nonreciprocity is a necessary ingredient for travelling wave generation, whereas global asymmetry controls global wave direction.

Modification in the manuscript:

“We should note that traveling waves indicate broken PT symmetry between these fields triggered by nonreciprocity, with spiral waves serving as a classic signature of this phenomenon. A further transition from spiral to planar waves reflects an overall asymmetry in the frequency profile, which is not directly related to PT-symmetry breaking.”

The relationship between the phase oscillator model and the active solid model is unclear. Given that U and P are both dynamical variables evolving in three-dimensional space, defining the phase Φ precisely in the phase space spanned by U and P could be challenging. A graphical illustration of the definition of Φ would be beneficial. To ensure reproducibility of the numerical results, the parameter values used in the numerical simulations and an explicit definition of the elastic force in the active solid model should be provided.

We agree with the reviewer that the relationship between the phase oscillator model and the active solid model can be confusing, but establishing this link is essential to connect different modeling approaches in the literature. As the reviewer notes, in a fully three-dimensional setting with freely moving bacteria, defining the oscillation phase (Φ) in the phase space spanned by U and P is indeed complicated.

However, our recent imaging results show that bacteria within the biofilm do not undergo large translational motions but instead exhibit periodic “Mexican wave”-like oscillations. These oscillations are confined to a restricted phase space, which allows us to define Φ in a straightforward way. In this context, the phase oscillator model becomes a natural reduction of the dynamics.

Similarly, in the active solid (or active gel) model, we can plot not only the displacement and force vectors but also the local phase, which shows strong agreement with the phenomenological Kuramoto-style model. To make this connection clearer, we have now included a schematic illustration in the revised manuscript that explicitly shows how Φ is defined in the reduced phase space, and we provide the parameter values used in the simulations as well as the explicit definition of the elastic force in the active solid model to ensure reproducibility.

The link between the theoretical models and experimental results is weak. For example, the propagation of the kink from the lower to the higher part of the surface (Figure 1e) could be addressed within the framework of the active solid model. The mechanism of transition from spiral to target waves (Figure 3a), b)) requires clarification, identifying which model parameter is crucial for inducing this transition. The wave propagation toward the lower frequency side is numerically demonstrated using the phase oscillator model, but a physical or intuitive explanation for this phenomenon is missing. Also, the wave transitions induced by the addition of water droplets and temperature rise are not linked to specific parameters in the theoretical models.

We thank the reviewer for highlighting this important weakness, which was also consistently noted by the other reviewers. We fully agree that the link between our theoretical models and experimental results required significant strengthening.

With improved imaging in the revised study, we were able to uncover additional connections that help establish this link more clearly. We acknowledge that our ability to measure detailed biofilm parameters is limited, which restricts us from providing fully quantitative mappings. Nonetheless, based on the reviewers’ suggestions, we carried out additional imaging and simulations to compare bacterial dynamics at the colony edge and within the biofilm surface. These data confirm that cells within the biofilm undergo restricted, “Mexican wave”-like oscillations, emphasizing the critical role of elasticity in governing the collective dynamics.

Experimentally, we found that adding water or PEG, or alternatively inducing drying, strongly modulates the effective elasticity of the biofilm. Within the active solid framework, elasticity and the elasto-active coupling are the key parameters controlling the system. By tuning these parameters in simulations, we could reproduce the qualitative transitions observed experimentally. Specifically, we observed that:

At low elasticity, topological defects are mobile and can move, merge, or annihilate, leading to the emergence of planar waves.

At high elasticity, defects remain pinned, across the biofilm surface, dominating the dynamics.

These observations suggest that the motility of defects is the crucial parameter governing the transition between spiral, target, and planar waves. Although we cannot independently manipulate each parameter in experiments, varying the moisture content provides an effective and experimentally accessible control.

Finally, our simulations and new analyses reveal that spiral defect cores can move and merge to form target waves or annihilate entirely—processes that we also observe experimentally. This rich dynamical behavior underscores the importance of elasticity in shaping pattern transitions, and we believe it warrants further theoretical exploration. We have clarified this connection and its implications in the revised manuscript.

First, we compare defect dynamics in both Kuramoto-based simulations and the active solid model. Both systems exhibit similar defect-survival behavior. As shown in the review , pairs of unlike (+/−) defects can stably persist only at high nonreciprocity. We further quantify this behavior by plotting the separation distances between unlike defect pairs and find that short-range defect separations are possible exclusively in the high-nonreciprocity regime Supplementary Figure 11.

This high-nonreciprocity regime corresponds to the dry biofilm state. Increasing moisture reduces elasticity, leading to the loss of stable defect dynamics and promoting the annihilation of unlike defect pairs, which in turn drives the system toward target-wave formation and ultimately planar waves. Conversely, heating the biofilm removes water, enhances elasticity, and increases the system’s ability to sustain closely separated defect pairs.

Experimentally, we further observe that removing water by heating enhances surface nonuniformities, which readily trigger defect-pair formation. To investigate this mechanism, we performed additional simulations in which local nonuniformities were introduced Supplementary Figure 12. Consistent with experiments, defect-pair generation occurs only at high nonreciprocity, where pairs of unlike defects can be stably maintained. Experimental observation (Author response image 4) also show that surface nonuniformities on the biofilm surface similarly trigger the formation of closely separated defect pairs. We have updated the details of the defect dynamics in the revised manuscript to clarify the transition between these waves.

Author response image 4.

Experimental observation showing that small surface nonuniformities on the biofilm surface trigger the formation of closely separated defect pairs. Arrows indicate the position of the nonuniformities

Modification in the manuscript:

Defect dynamics controlling the transition between spiral to target waves

“To better understand the dynamics of the transition between different form of the waves we focused on numerical simulations. We noticed that the motility of defects is the crucial parameter governing the transition between spiral, target, and planar waves varying the moisture content provides an effective and experimentally accessible control this motility. Our analyses revealed that spiral defect cores can move and merge to form target waves or annihilate entirely—processes that we also observe experimentally. This rich dynamical behavior underscores the importance of elasticity in shaping pattern transitions. First, we compare defect dynamics in both Kuramotobased simulations and the active solid model. Both systems exhibit similar defect-survival behavior. As shown in Supplementary Figure10, pairs of unlike (+/−) defects can stably persist only at high nonreciprocity. We further quantify this behavior by plotting the separation distances between unlike defect pairs and find that short-range defect separations are possible exclusively in the high-nonreciprocity regime (Supplementary Figure11). This high-nonreciprocity regime corresponds to the dry biofilm state. Increasing moisture reduces elasticity, leading to the loss of stable defect dynamics and promoting the annihilation of unlike defect pairs, which in turn drives the system toward target-wave formation and ultimately planar waves. Conversely, heating the biofilm removes water, enhances elasticity, and increases the system’s ability to sustain closely separated defect pairs. Experimentally, we further observe that removing water by heating enhances surface nonuniformities, which readily trigger defect-pair formation (Supplementary Video9). To investigate this mechanism, we performed additional simulations in which local nonuniformities were introduced (Supplementary Video12-13). Consistent with experiments, defect-pair generation occurs only at high nonreciprocity, where pairs of unlike defects can be stably maintained. Experimental observation (Supplementary Video9) also show that surface nonuniformities on the biofilm surface similarly trigger the formation of closely separated defect pairs.”

All the recommended points have been addressed in the revised manuscript.

eLife Assessment

This important study combines a two-person joint hand-reaching paradigm with game-theoretical modeling to examine whether, and how, reflexive visuomotor responses are modulated by a partner's control policy and cost structure. The study provides a convincing set of behavioral findings suggesting that involuntary visuomotor feedback is indeed modulated in the context of interpersonal coordination. The work will be of interest to cognitive scientists studying the motor and social aspects of action control.

Reviewer #1 (Public review):

Summary:

Sullivan and colleagues examined the modulation of reflexive visuomotor responses during collaboration between pairs of participants performing a joint reaching movement to a target. In their experiments, the players jointly controlled a cursor that they had to move towards narrow or wide targets. In each experimental block, each participant had a different type of target they had to move the joint cursor to. During the experiment, the authors used lateral perturbation of the cursor to test participants' fast feedback responses to the different target types. The authors suggest participants integrate the target type and related cost of their partner into their own movements, which suggests that visuomotor gains are affected by the partner's task.

Strengths:

The topic of the manuscript is very interesting, and the authors are using well-established methodology to test their hypothesis. They combine experimental studies with optimal control models to further support their work. Overall, the manuscript is very timely and shows important findings - that the feedback responses reflect both our and our partners tasks.

Reviewer #2 (Public review):

Summary:

Sullivan and colleagues studied the fast, involuntary, sensorimotor feedback control in interpersonal coordination. Using a cleverly designed joint-reaching experiment that separately manipulated the accuracy demands for a pair of participants, they demonstrated that the rapid visuomotor feedback response of a human participant to a sudden visual perturbation is modulated by his/her partner's control policy and cost. The behavioral results are well matched with the predictions of the optimal feedback control framework implemented with the dynamic game theory model. Overall, the study provides an important and novel set of results on the fast, involuntary feedback response in human motor control in the context of interpersonal coordination.

Review:

Sullivan and colleagues investigated whether fast, involuntary sensorimotor feedback control is modulated by the partner's state (e.g., cost and control policy) during interpersonal coordination. They asked a pair of participants to make a reaching movement to control a cursor and hit a target, where the cursor's position was a combination of each participant's hand position. To examine fast visuomotor feedback response, the authors applied a sudden shift in either the cursor (experiment 1) or the target (experiment 2) position in the middle of movement. To test the involvement of partner's information in the feedback response, they independently manipulated the accuracy demand for each participant by varying the lateral length of the target (i.e., a wider/narrower target has a lower/higher demand for correction when movement is perturbed). Because participants could also see their partner's target, they could theoretically take this information (e.g., whether their partner would correct, whether their correction would help their partner, etc.) into account when responding to the sudden visual shift. Computationally, the task structure can be handled using dynamic game theory, and the partner's feedback control policy and cost function are integrated into the optimal feedback control framework. As predicted by the model, the authors demonstrated that the rapid visuomotor feedback response to a sudden visual perturbation is modulated by the partner's control policy and cost. When their partner's target was narrow, they made rapid feedback corrections even when their own target was wide (no need for correction), suggesting integration of their partner's cost function. Similarly, they made corrections to a lesser degree when both targets were narrower than when the partner's target was wider, suggesting that the feedback correction takes the partner's correction (i.e., feedback control policy) into account.

The strength of the current paper lies in the combination of clever behavioral experiments that independently manipulate each participant's accuracy demand and a sophisticated computational approach that integrates optimal feedback control and dynamic game theory. Both the experimental design and data analysis sound good and the main claim is well supported by the results.

A future direction would be to investigate how this mechanism is implemented in the CNS and to examine whether the same cooperative mechanism also applies to human-AI interactions.

Author response:

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

Reviewer #1 (Public review):

Summary

Sullivan and colleagues examined the modulation of reflexive visuomotor responses during collaboration between pairs of participants performing a joint reaching movement to a target. In their experiments, the players jointly controlled a cursor that they had to move towards narrow or wide targets. In each experimental block, each participant had a different type of target they had to move the joint cursor to. During the experiment, the authors used lateral perturbation of the cursor to test participants’ fast feedback responses to the different target types. The authors suggest participants integrate the target type and related cost of their partner into their own movements, which suggests that visuomotor gains are affected by the partner’s task.

Strengths

The topic of the manuscript is very interesting, and the authors are using well established methodology to test their hypothesis. They combine experimental studies with optimal control models to further support their work. Overall, the manuscript is very timely and shows important findings - that the feedback responses reflect both our and our partner’s tasks.

We thank the reviewer for the positive comments regarding our work.

Weaknesses

However, in the current version of the manuscript, I believe the results could also be interpreted differently, which suggest that the authors should provide further support for their hypothesis and conclusions.

Major Comments

(1) Results of the relevant conditions:

In addition to the authors’ explanation regarding the results, it is also possible that the results represent a simple modulation of the reflexive response to a scaled version of cursor movement. That is, when the cursor is partially controlled by a partner, which also contributes to reducing movement error, it can also be interpreted by the sensorimotor system as a scaling of hand-to-cursor movement. In this case, the reflexes are modulated according to a scaling factor (how much do I need to move to bring the cursor to the target). I believe that a single-agent simulation of an OFC model with a scaling factor in the lateral direction can generate the same predictions as those presented by the authors in this study. In other words, maybe the controller has learned about the nature of the perturbation in each specific context, that in some conditions I need to control strongly, whereas in others I do not (without having any model of the partner). I suggest that the authors demonstrate how they can distinguish their interpretation of the results from other explanations.

We thank the reviewer for the thoughtful comment. While it is possible that the change in the visuomotor feedback responses could be just from a scaling factor. This hypothesis could explain the difference between two conditions, but would fail to explain differences between two other conditions. Specifically, this hypothesis could explain a decrease in involuntary visuomotor feedback responses between partner-irrelevant/self-relevant and partner-relevant/self-relevant. Critically, this hypothesis could not explain the difference between partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant. That is, there is no reason to scale a response to correct for a partner’s relevant target when your own target is irrelevant. However, our finding that there is a greater involuntary visuomotor feedback response in partner-relevant/self-irrelevant compared to partner-irrelevant/self-irrelevant is predicted by the notion that humans form a representation of others and consider their movement costs.

We have added a paragraph in the discussion to justify our hypothesis over the scaling factor hypothesis.

“Our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses can parsimoniously explain all of our experimental findings. There are a few alternative hypotheses that could explain a subset of results. One alternative hypothesis is that participants simply learned the hand to center cursor mapping in each experimental condition. That is, instead of using a model of their partner, participants simply adapted to the dynamics of the center cursor. However, this hypothesis would not predict an increased involuntary visuomotor feedback response in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-irrelevant condition. If participants did not form a model of their partner nor consider their partner’s costs, then they would not display an increased feedback response when they had an irrelevant target and their partner’s target was relevant. An increased feedback response to help a partner achieve their goal is captured by our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses.”

(2) The effect of the partner target:

The authors presented both self and partner targets together. While the effect of each target type, presented separately, is known, it is unclear how presenting both simultaneously affects individual response. That is, does a small target with a background of the wide target affect the reflexive response in the case of a single participant moving? The results of Experiment 2, comparing the case of partner- and self-relevant targets versus partner-irrelevant and self-relevant targets, may suggest that the system acted based on the relevant target, regardless of the presence and instructions regarding the self-target.

We thank the reviewer for bringing up another valid point, which we discussed at length as a group when designing the experiment. The reviewer is correct in pointing out the lack of difference in the involuntary epoch between the partner-relevant/self-relevant and partner-irrelevant/self-relevant could potentially suggest that the sensorimotor system acted based on only relevant targets, irrespective if it was a self or partner relevant target. While the effect of the simultaneous presentation of a narrow and wide target on an individual’s response by themselves is unknown, comparing the differences between our other experimental conditions control for this potential confound. Participants viewed a wide target and a narrow target on the screen, in both the partner-irrelevant/self-relevant condition and the partner-relevant/self-irrelevant condition. Crucially, we found that the visuomotor feedback responses were greater in the partner-irrelevant/self-relevant condition compared to the partner-relevant/self-irrelevant condition in both Experiment 1 and 2. That is, participants were able to distinguish between the self-target and partner target and appropriately modify their feedback responses in both Experiment 1 and 2, despite there being both a wide and narrow target on the screen in both conditions. Given that we found different visuomotor feedback responses between the two conditions that had both a narrow and wide target, this rules out the alternative hypothesis that the sensorimotor system acted based just on a relevant target being present. We have added to our discussion to clarify this point.

“Another alternative hypothesis would be that the sensorimotor system was responding only to the relevant target displayed on the screen. Again, this hypothesis would only explain a subset of our results. In particular, this relevant target hypothesis cannot explain the observed feedback response differences between the partner-relevant/self-irrelevant and partner-irrelevant/self-relevant conditions in both Experiments 1 and 2.”

(3) Experiment instructions:

It is unclear what the general instructions were for the participants and whether the instructions provided set the proposed weighted cost, which could be altered with different instructions.

Our instructions explicitly informed participants that their performance bonus was only based on them stabilizing within their own self-target within the time constraint. We have added the following in the methods to emphasize this instruction.

“In other words, we ensured participants had a clear understanding that their performance in the task was only based on stabilizing the center cursor in their own self-target within the time constraint. Therefore, the instructions and timing constraints did not enforce participants to work together.”

(4) Some work has shown that the gain of visuomotor feedback responses reflects the time to target and that this is updated online after a perturbation (Cesonis & Franklin, 2020, eNeuro; Cesonis and Franklin, 2021, NBDT; also related to Crevecoeur et al., 2013, J Neurophysiol). These models would predict different feedback gains depending on the distance remaining to the target for the participant and the time to correct for the jump, which is directly affected by the small or large targets. Could this time be used to target instead of explaining the results? I don’t believe that this is the case, but the authors should try to rule out other interpretations. This is maybe a minor point, but perhaps more important is the location (&time remaining) for each participant at the time of the jump. It appears from the figures that this might be affected by the condition (given the change in movement lengths - see Figure 3 B & C). If this is the case, then could some of the feedback gain be related to these parameters and not the model of the partner, as suggested? Some evidence to rule this out would be a good addition to the paper - perhaps the distance of each partner at the time of the perturbation, for example. In addition, please analyze the synchrony of the two partners’ movements.

(1) Time to target and forward position

The reviewer raises an interesting point. In our task, the cursor/target jump occurs once the center cursor crosses 6.25 cm from the start. We analyzed the time it took for the center cursor to intercept the targets from perturbation onset (Supplementary D). In Experiment 1, an ANOVA with center cursor time-to-target as the dependent variable showed no main effect of self-target (F[1,47] = 2.45, p = 0.124) or partner target (F[1,47] = 2.50, p=0.120), nor any interaction (F[1,47] = 1.97, p = 0.166). In Experiment 2, an ANOVA with center cursor time-to-target as the dependent variable showed a significant interaction (F[1,47] = 5.87, p = 0.019). Post-hoc mean comparisons showed that only the difference between the partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant condition was significant (p = 0.006). Given that only one comparison in Experiment 2 showed a difference in time-to-target, we do not believe that time-to-target was a significant driver of the change in involuntary visuomotor feedback responses observed between conditions. While time-to-target is likely a metric the nervous system modifies feedback gains around, our results suggest that the nervous system can also use a partner model to modify feedback gains. We have added a supplemental analysis on time to target

“Previous work by Česonis and Franklin (2020) showed that time to-target is a key variable the sensorimotor system uses to modify feedback responses. In their experiment, they manipulated the time-to-target of the participant’s cursor, while controlling for other movement parameters (e.g., distance from goal) [1]. When compared to classical optimal feedback control models, they showed that a model that modifies feedback responses based on time-to-target best predicted their results. In our task, it’s possible that the time-to-target could have influenced visuomotor feedback responses, since the distance to the center of the target is greater for a narrow target than a wide target on perturbation trials.”

“We calculated the time from perturbation onset to the center cursor reaching the forward position of the targets (Supplementary Fig. S5). In Experiment1, an ANOVA with center cursor time-to-target as the dependent variable showed no main effect of self-target (F[1,47]=2.45,p=0.124) or partner target (F[1,47] = 2.50, p=0.120), nor any interaction (F[1,47] = 1.97, p = 0.166). In Experiment2, an ANOVA with center cursor time-to-target as the dependent variable showed a significant interaction (F [1,47] = 5.87, p = 0.019). Post-hoc mean comparisons showed that only the difference between the partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant condition was significant (p=0.006). Although time-to-target and hand position are important variables for the control ofmovement,[1,2,3] they are likely not driving factors of the different in voluntary visuomotor feedback responses between our experimental conditions.”

However, it is possible that the participant forward position at perturbation onset could also influence the involuntary feedback response. We show the forward positions at perturbation onset in Supplementary D. Statistical analysis of the forward positions in Experiment 1 showed a main effect of self-target (F[1,47] = 12.72, p < 0.001), main effect of partner target (F[1,47] = 12.82, p < 0.001), and no interaction (F[1,47] = 0.00, P = 0.991). We see the same trend in experiment 2, showing a main effect of self-target (F[1,47] = 12.11, p < 0.001), main effect of partner target (F[1,47] = 12.04, p < 0.001), and no interaction (F[1,47] = 0.00, p = 0.986). The fact that there was no interaction implies that the results could not solely be due to forward position. Nevertheless, given there were main effects, we proceeded to run an ANCOVA on the involuntary visuomotor feedback responses with forward position as a covariate. For experiment 1, we still observed a significant interaction between self and partner target (F[1,47] = 43.14, p < 0.001). Further, we also observed no significant main effect of forward position on the involuntary visuomotor feedback responses. The ANCOVA for Experiment 2 also showed that there was still a significant interaction of self and partner target on the involuntary visuomotor feedback responses (F[1,47] = 9.80, p = 0.002). However, here we did find a significant main effect of the forward position (F[1,47] = 5.06, p = 0.026). Therefore, we ran follow-up mean comparisons with the covariate adjusted means. We found the same statistical trend as reported in the main results. We found significant differences between the partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant conditions (p = 0.003), partner-relevant/self-irrelevant and partner-irrelevant/self-relevant conditions (p < 0.001), partner-relevant/self-irrelevant and partner-relevant/self-relevant conditions (p < 0.001). We found no significant difference between the partner-irrelevant/self-relevant and partner-relevant/self-relevant conditions (p = 0.381). Given that there was no main effect of forward position in Experiment 1, and that our adjusted mean comparisons in Experiment 2 showed the same trends as the unadjusted mean comparisons in the main manuscript, our results show that the forward position of the participants is not a significant factor in explaining the differences in involuntary visuomotor feedback responses between conditions.

“Supplementary Fig. 6 shows the participant hand forward position at perturbation onset time for Experiment 1 (A) and Experiment 2 (B). It is possible that the participant forward hand position at perturbation onset time could influence their visuomotor feedback responses. Therefore, we ran an ANCOVA with self-target and partner target as factors, and participant forward hand position at perturbation onset time as a covariate. In Experiment 1, we found no main affect of participant forward hand position on involuntary visuomotor feedback responses (F[1,47] = 1.466, p = 0.228). Further, when including the covariate, we still found a significant interaction between self-target and partner target on in voluntary visuomotor feedback responses (F[1,47]=43.2, p<0.001).”

“In Experiment 2, we found a significant main effect of participant forward hand position on involuntary visuomotor feedback responses (F[1,47] = 6.73, p = 0.010). We still found a significant interaction between self-target and partner target (F[1,47] = 9.78, p = 0.002). Since we found a main effect of participant forward hand position, we calculated the adjusted means of the involuntary visuomotor feedback responses. We then performed follow-up mean comparisons on the adjusted means of the involuntary visuomotor feedback responses (using emmeans in R). We found the same significant trends as the unadjusted means in the main manuscript. Specifically we found involuntary visuomotor feedback responses to be: significantly greater in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-irrelevant condition (p =0.003),significantly greater in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-relevant condition (p<0.001), significantly greater in the partner-relevant/self-relevant condition compared to the partner-relevant/self-irrelevant condition (p<0.001),and not different between the partner-irrelevant/self-relevant and partner-relevant/self-relevant conditions (p = 0.824).”

We have also included in the discussion how time-to-target and participant forward hand position are important control variables to consider, and their potential relationship to our findings.

“Finally, we also considered whether time to target [1,2]. (Supplementary D), participant forward hand position (Supplementary E), or learning [4] (Supplementary G-H) influenced feedback responses, but found that none impacted the observed differences between experimental conditions nor changed our interpretation. Our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses parsimoniously accounts for the differences observed between all conditions.”

(2) Synchrony

In our task, participants movements were not self-initiated. We had them begin the movement as soon as they hear an audible tone so that they would begin their movements at as similar a time as possible. We have analyzed the movement onset synchrony between participants within a pair, shown in Supplementary F.

Supplementary: “We calculated movement onset times at the time that the participants left the start target [8]. We then took the absolute value of the difference between the participants within a pair as a measure of movement onset synchrony. For Experiment 1, an ANOVA with movement onset synchrony as the dependent variable showed no main effect of self-target (F[1,47] = 1.38, p = 0.252), no main effect of partner target (F[1,47] = 0.057, p = 0.813), and no interaction (F[1,47] = 0.45, p = 0.508). For Experiment 2, an ANOVA with movement onset synchrony as the dependent variable showed no main effect of self-target (F[1,47] = 0.07, p = 0.788), no main effect of partner target (F[1,47] = 2.75, p = 0.111), and no interaction (F[1,47] = 2.31, p = 0.142).”

Further, we have modified our methods to emphasize that participants within a pair generally began their movement at the same time.

“Instead of self-initiating their movements, we specifically had participants move at the sound of a tone so that the movement onset between participants in a pair was as synchronous as possible (see Supplementary F for movement onset synchrony analysis).”

Reviewer #1 (Recommendations for the authors):

(1) Lines 291-292: One study extensively examined cursor and target jump visuomotor on set times and found no difference (Franklin et al., 2016; J Neuroscience), which strongly argues against this interpretation.

We thank the reviewer for pointing out this work. We have modified the following lines:

“However, other work by Franklin and colleagues (2016) found no difference in visuomotor feedback response latencies between cursor and target jumps [6].”

(2) Line 411: What were the instructions regarding partner performance in terms of the reward? Did you explain that individual performance alone will determine the reward?

As addressed above, we have made the following changes to emphasize the instructions given to participants.

“In other words, we ensured participants had a clear understanding that their performance in the task was only based on stabilizing the center cursor in their own self-target within the time constraint. Therefore, the instructions and timing constraints did not enforce participants to work together.”

(3) Line 506: Ten probe trials in each direction is very low. Can this still be in the transition state of the feedback response, rather than at steady state? There are many studies done looking at the learning of visuomotor responses in which changes are still occurring after several hundred trials (e.g., Franklin et al., 2017 J Neurophysiol; Franklin et al., 2008; J Neuroscience). In this experiment, each block only lasts 151 trials total if my calculations are correct. How certain are you that the results are at a steady state and not continuously changing? Perhaps with further experimental experience, the feedback responses would approach the predictions of a different model.

The reviewer raises an important point. We had run these analyses prior to submitting the manuscript and did not see anything. However, we believe this information is important to include since both we and yourself asked the same question. Specifically, we have analyzed the visuomotor feedback responses over the trials (Supplementary G), which shows little to no learning over time. Additionally, we also found no difference in the visuomotor feedback response trends between the first and second half of trials in each condition (Supplementary H). Therefore, it appears that the sensorimotor system was at steady state behaviour very quickly and we do believe that the feedback responses would approach the predictions of a different model if participants performed more trials. We have added the following

Supplementary: “Given there were 151 trials and 10 left/right probe trials for each experimental condition, it is possible that completing more trials may have lead to different involuntary visuomotor feedback responses. Therefore, we analysed the in voluntary visuomotor feedback responses over the course of each experimental condition. Visually, involuntary visuomotor feedback responses in neither Experiment 1 (Fig. S8) nor Experiment 2 (Fig. S9) show any consistent learning (see Fig. S10 for statistical analysis). Therefore, it appears participants rapidly formed a partner model based on knowledge of their movement goal to modify their involuntary visuomotor feedback responses.”

Supplementary: “Supplementary Fig. S10 shows the involuntary visuomotor feedback responses in the first half (A,C) and second half (B,D) for each experimental condition. In Experiment 1, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 37.09, p < 0.001) and second half (F[1,47] = 48.68, p < 0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (see Fig. S10A-B).”

Supplementary: “In Experiment 2, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 9.42, p = 0.004) and second half (F[1,47] = 17.40, p < 0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (Fig. S10C-D).”

Supplementary: “Showing the same involuntary visuomotor feedback response trends across the experimental conditions for the first half, second half, and all trials suggests that the sensorimotor system quickly formed a model of a partner and considered their costs to modify rapid motor responses.”

We have also added to the discussion:

“Finally, we also considered whether time to target [1,2] (Supplementary D), participant forward hand position (Supplementary E), or learning [4] (Supplementary G) influenced feedback responses, but found that none impacted the observed differences between experimental conditions nor changed our interpretation.”

(4) The authors should also discuss some of the prior work which is very relevant to the tasks studied: (Knill, Bondata & Chhabra, 2011, J Neuroscience). There may also be other papers that use this task for visuomotor feedback responses and therefore, should be included.

We have included the Knill 2011 paper and also Cross 2019 in our discussion:

“This modification of feedback responses based on a relevant/irrelevant task goal has also been shown in response to visual perturbations [7,8].”

(5) Lines 301-303: The terms ’relevant’ and ’irrelevant’ here describe different concepts than the ones used in this study. I suggest making a distinction to avoid confusion for the reader.

We thank the reviewer for pointing out that this is confusing. We’ve made the following changes to improve the clarity:

“Further, Franklin and colleagues (2008) designed a visual perturbation to be relevant or irrelevant when reaching to the same target, showing greater involuntary visuomotor feedback responses to a relevant visual perturbation compared to an irrelevant visual perturbation [9].”

(6) Line 459: The reaching movement was quite slow (25cm in about 1.2 seconds). Is this needed to ensure that both participants can complete the movements, given potentially very different start times? Please comment as this is different than many previous studies.

Participants needed to stabilize the cursor for 500ms in their target within a time constraint of 1400 - 1600 ms. Therefore, they had to reach the target between 900 - 1100 ms (before stabilizing). Additionally, participants did not perform self-initiated movements, but were required to begin their movement as soon as they heard an audible tone. Given that reaction times are ~200ms, participants had ~700 - 900 ms to reach the target, which aligns with previous research (Franklin et al. (2008), Franklin et al. (2012), Nashed et al. (2012)). We have clarified the time constraints of the task in our Methods:

“They therefore had 700 - 900 ms to first reach the target, since humans generally have response times ~200 ms, and they needed to stabilize within the target for 500 ms (i.e., 1400 - 200 - 500 = 700 ms and 1600 - 200 - 500 = 900 ms). Movement times of 700 - 900 ms are thus consistent with previous human reaching studies [4,9,10].”

(7) Reference [25] is incomplete

Thank you for catching this.

And thank you for the thoughtful and clear review. We feel it has greatly improved the quality and clarity of our manuscript!

Reviewer #2 (Public review):

Summary

Sullivan and colleagues studied the fast, involuntary, sensorimotor feedback control in interpersonal coordination. Using a cleverly designed joint-reaching experiment that separately manipulated the accuracy demands for a pair of participants, they demonstrated that the rapid visuomotor feedback response of a human participant to a sudden visual perturbation is modulated by his/her partner’s control policy and cost. The behavioral results are well-matched with the predictions of the optimal feedback control framework implemented with the dynamic game theory model. Overall, the study provides an important and novel set of results on the fast, involuntary feedback response in human motor control, in the context of interpersonal coordination.

We thank the reviewer for the kind words!

Review:

Sullivan and colleagues investigated whether fast, involuntary sensorimotor feedback control is modulated by the partner’s state (e.g., cost and control policy) during interpersonal coordination. They asked a pair of participants to make a reaching movement to control a cursor and hit a target, where the cursor’s position was a combination of each participant’s hand position. To examine fast visuomotor feedback response, the authors applied a sudden shift in either the cursor (experiment 1) or the target (experiment 2) position in the middle of movement. To test the involvement of partner’s information in the feedback response, they independently manipulated the accuracy demand for each participant by varying the lateral length of the target (i.e., a wider/narrower target has a lower/higher demand for correction when movement is perturbed). Because participants could also see their partner’s target, they could theoretically take this information (e.g., whether their partner would correct, whether their correction would help their partner, etc.) into account when responding to the sudden visual shift. Computationally, the task structure can be handled using dynamic game theory, and the partner’s feedback control policy and cost function are integrated into the optimal feedback control framework. As predicted by the model, the authors demonstrated that the rapid visuomotor feedback response to a sudden visual perturbation is modulated by the partner’s control policy and cost. When their partner’s target was narrow, they made rapid feedback corrections even when their own target was wide (no need for correction), suggesting integration of their partner’s cost function. Similarly, they made corrections to a lesser degree when both targets were narrower than when the partner’s target was wider, suggesting that the feedback correction takes the partner’s correction (i.e., feedback control policy) into account.

The strength of the current paper lies in the combination of clever behavioral experiments that independently manipulate each participant’s accuracy demand and a sophisticated computational approach that integrates optimal feedback control and dynamic game theory. Both the experimental design and data analysis sound good. While the main claim is well-supported by the results, the only current weakness is the lack of discussion of limitations and an alternative explanation. Adding these points will further strengthen the paper.

Reviewer #2 (Recommendations for the authors):

(1) While the current version is already well-written, it would be helpful for readers to further discuss the relationship between the current study and some potentially relevant studies, such as Braun et al. (2009), Ganesh et al. (2014), and Takagi et al. (2017) (2019).

Thank you for pointing out these papers that we missed, which we now cite appropriately in light of our own work. In particular, we have added the following to our discussion, including Braun et al. (2009) and Takagi et al. (2017) (2019). However, Beckers et al. (2020) showed conflicting results from Ganesh et al. (2014), and since these works are about learning, we feel it is outside the scope of our work.

“Further, others have shown that the sensorimotor system modifies movement selection according to game-theoretic predictions, [11] and that the sensorimotor system modifies movements using an estimate of the joint goal during human-human interactions [12,13].”

(2) For an alternative interpretation of the results, one could consider, for instance, that the target’s visual appearance could have served as a contextual cue for learning different movement gains in the lateral direction (e.g., whether the partner corrects the shift might be approximated as a gain change). Although less likely, this alternative account could be tested by simulation and would strengthen the argument.

This a thoughtful comment, also brought up by Reviewer 1. Here we provide our previous response that addresses this concern. While it is possible that the change in the visuomotor feedback responses could be just from a scaling factor. This hypothesis could explain the difference between two conditions, but would fail to explain differences between two other conditions. Specifically, this hypothesis could explain a decrease in involuntary visuomotor feedback responses between partner-irrelevant/self-relevant and partner-relevant/self-relevant. Critically, this hypothesis could not explain the difference between partner-irrelevant/self-irrelevant and partner-relevant/self-irrelevant. That is, there is no reason to scale a response to correct for a partner’s relevant target when your own target is irrelevant. However, our finding that there is a greater involuntary visuomotor feedback response in partner-relevant/self-irrelevant compared to partner irrelevant/self-irrelevant is predicted by the notion that humans form a representation of others and consider their movement costs.

We have added a paragraph in the discussion to justify our hypothesis over the scaling factor hypothesis.

“Our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses can parsimoniously explain all of our experimental findings. There are a few alternative hypotheses that could explain a subset of results. One alternative hypothesis is that participants simply learned the hand to center cursor mapping in each experimental condition. That is, instead of using a model of their partner, participants simply adapted to the dynamics of the center cursor. However, this hypothesis would not predict an increased involuntary visuomotor feedback response in the partner-relevant/self-irrelevant condition compared to the partner-irrelevant/self-irrelevant condition. If participants did not form a model of their partner nor consider their partner’s costs, then they would not display an increased feedback response when they had an irrelevant target and their partner’s target was relevant. An increased feedback response to help a partner achieve their goal is captured by our hypothesis that the sensorimotor system uses a representation of a partner and considers the partner’s costs to modify involuntary visuomotor feedback responses.”

(3) Another (maybe unlikely) alternative interpretation is that the targets’ visual appearances might have been confusing. One might find that the closed square is common to both targets for the “Partner Relevant Self Irrelevant” and the “Partner Relevant Self Relevant”, and that this might have elicited the response to perturbation in “Partner Relevant Self Irrelevant”. Related to this point, it would be informative to describe how the “cooperative” fast feedback response developed over the course of the experiment, for instance, by comparing behaviors across experimental blocks.

We have partitioned this question into two responses, relating to visual appearance of the targets and the development (i.e., learning) of visuomotor feedback responses over the course of the experiments.

(1) Participants confused by visual appearance of the targets.

We were also concerned that participants might be confused by the targets, and therefore confirmed with participants after the experiment that they correctly understood that the light grey filled rectangle was their own target and the dark grey hollow rectangle was their partners. Furthermore, in the partner-relevant/self-irrelevant, partner-irrelevant/self-relevant, and partner-relevant/self-relevant conditions, there is a small square target in each of the conditions. However, we found that the partner-irrelevant/self-relevant and partner-relevant/self-relevant conditions both elicited significantly greater involuntary visuomotor feedback responses than the partner-relevant/self-irrelevant condition. Thus, participants involuntary visuomotor feedback responses suggest that they correctly formed different representations based on an accurate understanding of the self vs partner target. The other reviewer had related comments about the visual stimuli, which we also address within the discussion.

“Another alternative hypothesis would be that the sensorimotor system was responding only to the relevant target displayed on the screen. Again, this hypothesis would only explain a subset of our results. In particular, this relevant target hypothesis cannot explain the observed differences between the partner-relevant/self-irrelevant and partner-irrelevant/self-relevant conditions in both Experiments 1 and 2.”

(2) Comparing feedback responses over time

We have included the visuomotor feedback responses over each experimental condition in Supplementary G. Notably, we did not find any learning effect, suggesting that the sensorimotor system quickly developed a model of a partner’s behaviour and used that model to modify feedback responses. We have also added a paragraph on learning to our discussion.

We’ve addressed how learning did not play a role in this study:

“Finally, we also considered whether time to target [1,2] (Supplementary D), participant forward hand position (Supplementary E), or learning [4] (Supplementary G-H) influenced feedback responses, but found that none impacted the observed differences between experimental conditions nor changed our interpretation.”

Supplementary: “Given there were 151 trials and 10 left/right probe trials for each experimental condition, it is possible that completing more trials may have lead to different in voluntary visuomotor feedback responses. Therefore, we analysed the in voluntary visuomotor feedback responses over the course of each experimental condition. Visually, involuntary visuomotor feedback responses in neither Experiment 1 (Fig. S8) nor Experiment 2 (Fig. S9) show any consistent learning (see Fig. S10 for statistical analysis). Therefore, it appears participants rapidly formed a partner model based on knowledge of their movement goal to modify their involuntary visuomotor feedback responses.”

Supplementary: “Supplementary Fig. S10 shows the involuntary visuomotor feedback responses in the first half (A,C) and second half (B,D) for each experimental condition. In Experiment 1, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 37.09, p < 0.001) and second half (F[1,47] = 48.68, p < 0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (see Fig. S10A-B).”

Supplementary: “Supplementary Fig. S10 shows the involuntary visuomotor feedback responses in the first half (A,C) and second half (B,D) for each experimental condition. In Experiment 1, we observed the same statistical results in the first half and second half of trials as the analysis of all trials. That is, we observed a significant interaction between self-target and partner target in the first half (F[1,47] = 37.09, p < 0.001) and second half (F[1,47] = 48.68, p <0.001) of trials. Follow-up mean comparisons showed the same significant trends as our analysis of all trials in the main manuscript (see Fig. S10A-B).”

Supplementary: “Showing the same involuntary visuomotor feedback response trends across the experimental conditions for the first half, second half, and all trials suggests that the sensorimotor system used a model of a partner based on their goals and considered their costs to modify rapid motor responses.”

(4) It looks slightly counter intuitive (and therefore interesting) that the participant shows some amount of fast feedback responses in the “Partner Relevant Self Irrelevant” condition, since they were instructed to only consider the self-target. Based on the results, the authors suggest an altruistic feature of the motor system (lines 333-340). It would be helpful to clarify the basis for this interpretation, whether it is formally derived from the game-theoretic framework or represents a more conceptual interpretation. Providing additional explanation that translates the game-theoretic reasoning into more accessible, intuitive terms would help readers better understand and evaluate this claim.

We are glad the reviewer also finds this result interesting. The reviewer raises an important point that there needs to be a more clear explanation for why we believe this result was found. We have made the following changes to the discussion:

“Furthermore, this result is predicted by our dynamic game theory models that include the partner’s costs in the self cost function. In other words, a dynamic game theory model that selects feedback gains to minimize both the self and partner cost reflects an altruistic control policy.”

(5) Please check whether all references are displayed correctly. Some of them (e.g., 25, 65) seemed not correctly shown in the References section.

We have fixed the citation.

We thank the reviewer for providing a clear and insightful review. Their comments have significantly improved the manuscript.

References

(1) Česonis, J., & Franklin, D. W. (2020). Time-to-Target Simplifies Optimal Control of Visuomotor Feedback Responses. eneuro, 7 (2), ENEURO.0514–19.2020.

(2) Česonis, J., & Franklin, D. W. (2022). Contextual Cues Are Not Unique for Motor Learning: Task-dependant Switching of Feedback Controllers. PLOS Computational Biology, 18 (6), ed. by Haith, A. M.: e1010192.

(3) Crevecoeur, F., Kurtzer, I., Bourke, T., & Scott, S. H. (2013). Feedback Responses Rapidly Scale with the Urgency to Correct for External Perturbations. Journal of Neurophysiology, 110 (6), 1323–1332.

(4) Franklin, S., Wolpert, D. M., & Franklin, D. W. (2012). Visuomotor Feedback Gains Upregulate during the Learning of Novel Dynamics. Journal of Neurophysiology, 108 (2), 467–478.

(5) Liu, Y., Leib, R., Dudley, W., Shafti, A., Faisal, A. A., & Franklin, D. W. (2025). Partner-Sourced Haptic Feedback Rather than Environmental Inputs Drives Coordination Improvement in Human Dyadic Collaboration. Scientific Reports, 15 (1), 40347.

(6) Franklin, D. W., Reichenbach, A., Franklin, S., & Diedrichsen, J. (2016). Temporal Evolution of Spatial Computations for Visuomotor Control. The Journal of Neuroscience, 36 (8), 2329–2341.

(7) Knill, D. C., Bondada, A., & Chhabra, M. (2011). Flexible, Task-Dependent Use of Sensory Feedback to Control Hand Movements. The Journal of Neuroscience, 31 (4), 1219–1237.

(8) Cross, K. P., Cluff, T., Takei, T., & Scott, S. H. (2019). Visual Feedback Processing of the Limb Involves Two Distinct Phases. The Journal of Neuroscience, 39 (34), 6751–6765.

(9) Franklin, D. W., & Wolpert, D. M. (2008). Specificity of Reflex Adaptation for Task-Relevant Variability. The Journal of Neuroscience, 28 (52), 14165–14175.

(10) Nashed, J. Y., Crevecoeur, F., & Scott, S. H. (2012). Influence of the Behavioral Goal and Environmental Obstacles on Rapid Feedback Responses. Journal of Neurophysiology, 108 (4), 999–1009.

(11) Braun, D. A., Ortega, P. A., & Wolpert, D. M. (2009). Nash Equilibria in Multi-Agent Motor Interactions. PLoS Computational Biology, 5 (8), ed. by Friston, K. J.: e1000468.

(10) Takagi, A., Ganesh, G., Yoshioka, T., Kawato, M., & Burdet, E. (2017). Physically Interacting Individuals Estimate the Partner’s Goal to Enhance Their Movements. Nature Human Behaviour, 1 (3), 0054.

(11) Takagi, A., Hirashima, M., Nozaki, D., & Burdet, E. (2019). Individuals Physically Interacting in a Group Rapidly Coordinate Their Movement by Estimating the Collective Goal. eLife, 8 , e41328.

eLife Assessment

This study addresses an important question and shows how social navigation in homing pigeons can be explained by simple averaging, without requiring any complex cognitive abilities. The evidence, based on a rigorous and systematic comparison of seven models and data on how social routes can be generated from solitary routes, is compelling. The authors should be commended for their willingness to critically re-examine established interpretations.

Reviewer #1 (Public review):

Summary:

This study investigates how collective navigation improvements arise in homing pigeons. Building on the Sasaki & Biro (2017) experiment on homing pigeons, the authors use simulations to test seven candidate social learning strategies of varying cognitive complexity, ranging from simple route averaging to potentially cognitively demanding selective propagation of superior routes. They show that only the simplest strategy-equal route averaging-quantitatively matches the experimental data in both route efficiency and social weighting. More complex strategies, while potentially more effective, fail to align with the observed data. The authors also introduce the concept of "effective group size," showing that the chaining design leads to a strong dilution of earlier individuals' contributions. Overall, they conclude that cognitive simplicity rather than cumulative cultural evolution explains collective route improvements in pigeons.

Strengths:

The manuscript provides a compelling argument that a simpler hypothesis is necessary and sufficient to explain the findings of a recent study on improvements to pigeon routes, through a rigorous, systematic comparison of seven alternative hypotheses. The authors should be commended for their willingness to critically re-examine established interpretations. The introduction and discussion are broad and link pigeon navigation to general debates on social learning, wisdom of crowds, and CCE.

Weaknesses:

The authors' method focuses on trajectory-level average behaviour rather than the fine-scale decision-making processes of organisms. This is acknowledged in the manuscript by the authors.

Comments on revision:

The authors have addressed most of the comments by me as well as the other reviewer.

Reviewer #2 (Public review):

Summary:

The manuscript investigates which social navigation mechanisms, with different cognitive demands, can explain experimental data collected from homing pigeons. Interestingly, the results indicate that the simplest strategy - route averaging - aligns best with the experimental data, while the most demanding strategy - selectively propagating the best route - offers no advantage. Further, the results suggest that a mixed strategy of weighted averaging may provide significant improvements.

The manuscript addresses the important problem of identifying possible mechanisms that could explain observed animal behavior by systematically comparing different candidate models. A core aspect of the study is the calculation of collective routes from individual bird routes using different models that were hypothesized to be employed by the animals but which differ in their cognitive demands.

The manuscript is well written, with high-quality figures supporting both the description of the approach taken and the presentation of results. The results should be of interest to a broad community of researchers investigating (collective) animal behavior, ranging from experiment to theory. The general approach and mathematical methods appear reasonable and show no obvious flaws. The statistical methods also appear.

Strengths:

The main strength of the manuscript is the systematic comparison of different meta-mechanisms for social navigation by modeling social trajectories from solitary trajectories and directly comparing them with experimental results on social navigation. The results show that the experimentally observed behavior could, in principle, arise from simple route averaging without the need to identify "knowledgeable" individuals. Another strength of the work is the establishment of a connection between social navigation behavior and the broader literature on the wisdom of crowds through the concept of effective group size.

Comments on revision:

The authors made substantial revisions to the manuscript, addressing my comments. While I do think that regarding my second comment on CCE the authors could be a bit more bold, I am overall satisfied with the revisions made.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates how collective navigation improvements arise in homing pigeons. Building on the Sasaki & Biro (2017) experiment on homing pigeons, the authors use simulations to test seven candidate social learning strategies of varying cognitive complexity, ranging from simple route averaging to potentially cognitively demanding selective propagation of superior routes. They show that only the simplest strategy-equal route averaging-quantitatively matches the experimental data in both route efficiency and social weighting. More complex strategies, while potentially more effective, fail to align with the observed data. The authors also introduce the concept of "effective group size," showing that the chaining design leads to a strong dilution of earlier individuals' contributions. Overall, they conclude that cognitive simplicity rather than cumulative cultural evolution explains collective route improvements in pigeons.

Strengths:

The manuscript addresses an important question and provides a compelling argument that a simpler hypothesis is necessary and sufficient to explain findings of a recent influential study on pigeon route improvements, via a rigorous systematic comparison of seven alternative hypotheses. The authors should be commended for their willingness to critically re-examine established interpretations. The introduction and discussion are broad and link pigeon navigation to general debates on social learning, wisdom of crowds, and CCE.

We thank the reviewer for their positive comments.

Weaknesses:

The lack of availability of codes and data for this manuscript, especially given that it critically examines and proposes alternative hypotheses for an important published work.

We thank the reviewer for their comment. The code and data for our manuscript are an important aspect of the study, and we had intended to make them publicly available upon publication. The link to our code and data on fig share can be found here: (https://doi.org/10.6084/m9.figshare.28950032.v1). We have now revised the manuscript to include a link to our dataset.

Reviewer #2 (Public review):

Summary:

The manuscript investigates which social navigation mechanisms, with different cognitive demands, can explain experimental data collected from homing pigeons. Interestingly, the results indicate that the simplest strategy - route averaging - aligns best with the experimental data, while the most demanding strategy - selectively propagating the best route - offers no advantage. Further, the results suggest that a mixed strategy of weighted averaging may provide significant improvements.

The manuscript addresses the important problem of identifying possible mechanisms that could explain observed animal behavior by systematically comparing different candidate models. A core aspect of the study is the calculation of collective routes from individual bird routes using different models that were hypothesized to be employed by the animals, but which differ in their cognitive demands.

The manuscript is well-written, with high-quality figures supporting both the description of the approach taken and the presentation of results. The results should be of interest to a broad community of researchers investigating (collective) animal behavior, ranging from experiment to theory. The general approach and mathematical methods appear reasonable and show no obvious flaws. The statistical methods also appear.

Strengths:

The main strength of the manuscript is the systematic comparison of different meta-mechanisms for social navigation by modeling social trajectories from solitary trajectories and directly comparing them with experimental results on social navigation. The results show that the experimentally observed behavior could, in principle, arise from simple route averaging without the need to identify "knowledgeable" individuals. Another strength of the work is the establishment of a connection between social navigation behavior and the broader literature on the wisdom of crowds through the concept of effective group size.

We thank the reviewer for their positive comments.

Weaknesses:

However, there are two main weaknesses that should be addressed:

(1) The first concerns the definition of "mechanism" as used by the authors, for example, when writing "navigation mechanism." Intuitively, one might assume that what is meant is a behavioral mechanism in the sense of how behavior is generated as a dynamic process. However, here it is used at a more abstract (meta) level, referring to high-level categories such as "averaging" versus "leader-follower" dynamics. It is not used in the sense of how an individual makes decisions while moving, where the actual route followed in a social context emerges from individuals navigating while simultaneously interacting with conspecifics in space and time. In the presented work, the approach is to directly combine (global) route data of solitary birds according to the considered "meta-mechanisms" to generate social trajectories. Of course, this is not how pigeon social navigation actually works-they do not sit together before the flight and say, "This is my route, this is your route, let's combine them in this way." A mechanistic modeling approach would instead be some form of agent-based model that describes how agents move and interact in space and time. Such a "bottom-up" approach, however, has its drawbacks, including many unknown parameters and often strongly simplifying (implicit) assumptions. I do not expect the authors to conduct agent-based modeling, but at the very least, they should clearly discuss what they mean by "mechanism" and clarify that while their approach has advantages-such as naturally accounting for the statistical features of solitary routes and allowing a direct comparison of different meta-mechanisms is also limited, as it does not address how behavior is actually generated. For example, the approach lacks any explicit modeling of errors, uncertainty, or stochasticity more broadly (e.g., due to environmental influences). Thus, while the presented study yields some interesting results, it can only be considered an intermediate step toward understanding actual behavioral mechanisms.

We thank the reviewer for their comment and thoughtful suggestions. We agree that the inherent behavioral mechanisms and the biological basis of these mechanisms cannot be determined just through the navigational data alone. For instance, it remains unexplored if pigeons are adapting their behavior based only on social cues from their partners or using other navigational features such as landmarks or roads, location of the sun, geomagnetic cues or prior learnt routes. However, we do agree (as also pointed by the reviewer) that these behavioral rules generate an emergent ‘meta-mechanism’ where the bird pairs are behaving as if their preferred routes are averaged during a flight. It will be important in future work to explore the biological basis of these mechanisms, but our current approach allows us to only describe the mechanisms in a meta sense with any confidence. Considering this, we believe that our analysis is a more top-down approach towards describing the outcomes of these underlying mechanisms in an abstract sense. We would also like to point the reviewer to Dalmaijer, 2024 [1] who used a bottom up approach, using naive agents and showed that cumulative route improvements emerged in the absence of any sophisticated communication in the same dataset, in agreement with our approach. We have now added a paragraph: “It is also important to clarify that we use the terms…… that lead to these meta-mechanisms arising remain an open question.” found in lines 120-129 in our Introduction to make this clarification.

(2) While the presented study raises important questions about the applicability and viability of cumulative cultural evolution (CCE) in explaining certain animal behaviors such as social navigation, I find that it falls short in discussing them. What are the implications regarding the applicability of CCE to animal data and to previously claimed experimental evidence for CCE? Should these experiments be re-analyzed or critically reassessed? If not, why? What are good examples from animal behavior where CCE should not be doubted? Furthermore, what about the cited definitions and criteria of CCE? Are they potentially too restrictive? Should they be revised-and if so, how? Conversely, if the definitions become too general, is CCE still a useful concept for studying certain classes of animal behavior? I think these are some of the very important questions that could be addressed or at least raised in the discussion to initiate a broader debate within the community.

We thank the reviewer for their comments and interesting questions regarding our study. We agree with the reviewer that our study opens up new avenues for critically analysing the criteria previous studies have used for providing evidence of CCE in non-human animals. According to our literature review, we found that the field has been usually motivated in thinking about CCE in a ‘process’ focused manner (Reindl et al. [2]) in regards to individuals being able to compare strategies and selecting ones resulting in higher individual fitness. This preferential selection of strategies – termed innovations — allows for the stereotypical ratcheting effect seen in CCE. In our study, we propose that in the case of homing pigeons, the ratcheting effect is more of a statistical outcome rather than deliberate individual judgement. We believe that this strategy is also amenable to certain task types (which in our study was homing route choice) and may change for others (for example solving a puzzle box) and the task also needs to be sufficiently complex for animals to benefit from the use of social information (Caldwell et al. 2008 [3]). Thus, we recommend future work to address what classes of problems would fit well within the definition of “emergent” CCE and which ones don’t. Keeping this framework in mind, studies should clearly state what definition of CCE they are using and should be critically evaluated for their underlying task type and cognitive mechanisms to deem them as CCE. Considering these points, we have now expanded our Discussion to include a paragraph: “Our results highlight the need for more…..range of task types and cognitive abilities.” found in lines 420-433 to highlight these key questions.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I do not have any major objections, but I am clarifying my points as major or minor depending on the effort required to address (mostly via rewriting and clarifications).

Major comments:

(1) A schematic summary of the original study: Since the current manuscript builds directly on Sasaki & Biro (2017), it would greatly help readers if you included a concise schematic figure summarizing the original experiment. For instance, a simple panel could depict the chain design (experienced + naïve replacements), the control treatments, and the key empirical findings (improvements in route efficiency across generations, and route similarity within vs. between chains). Presenting this visually would save readers the effort of reconstructing the design and main results from text alone, especially for those unfamiliar with the original paper. It would also clarify exactly what empirical patterns your simulations are intended to reproduce.

We thank the reviewer for this comment. We have now revised the manuscript with a schematic illustration adapted from the original study by Sasaki and Biro (2017). We hope this clarifies the experimental design and results we aimed to highlight in our work.

(2) Reproducibility: Code and data are only "available on request." I believe eLife has strong policies on open science; a lack of immediate open access to analysis would be a barrier. I find it jarring that a paper intending to reproduce and improvise a previously published paper does not make the codes and data available for peer review or to readers without an explicit request.

We have taken the feedback into consideration and updated the Data Availability section with a link to our Fig share dataset.

(3) One huge drawback of the current format of the manuscript, where Methods come after Results, is that one has to really struggle to understand and appreciate Figures 2 and 3. I would strongly urge authors to have a shorter methods section embedded either as a subsection before the Results, or within the results section, as described in each figure. Perhaps a lot of my confusion also comes from not having known the previous paper, but it may be true for other readers, too. More specifically, for Figure 3, how is social weight for the experiments inferred? Figure 3 caption talks of mean difference, but one has to check the manuscript at multiple places throughout to really understand what this difference is (the definition) and how it is computed.

While we agree that our manuscript includes the Methods section at the end, we tried to structure our text to tell a story (as stated in our manuscript title). To this end, we organized the text into short titled subsections that briefly convey the relevant background, identify the knowledge gap and outline our approach. We chose this structure to reserve the indepth details about model implementation and statistical analysis for the Methods.

Additionally, we made sure to include references to methodological details in relevant segments of the Introduction and Results section so as to not bog down the reader by model complexities and keep a coherent narrative that delivers the message of our study. To further address the background of our work, we have now added a schematic of the original study in response to a previous comment by the reviewer, which we hope helps the reader better understand our work. We hope this explanation clarifies the intention behind our writing choice and decision to retain the current structure.

(4) The introduction of the 'effective group size' concept is a potentially valuable and intuitive way to interpret chain dynamics, but the explanation is somewhat buried in the Results/Methods; I suggest highlighting it more prominently (e.g., in the Discussion or with a schematic in the Results) so readers can readily grasp this useful idea.

We thank the reviewer that they found our concept of ‘effective group size’ useful. However, we do believe that we introduced the idea and rationale behind using this method in the Results: “We asked to what extent……to an equivalent group size” found in lines 305-314. We reserved a detailed description of this method in the Methods section. However, to further emphasize the importance of the concept we have now added a text: “This is further supported….. slightly better than two individuals.” found in lines 389-394 in the Discussion. 

Minor comments:

(1) Line 12: "what is the navigation mechanism(s)" - the (s) is a bit awkward. Either remove (s) or ask what the mechanisms are.

We have fixed the typo to clarify the statement.

(2) Line 78: "Such 'ratchet'-like improvements is referred to..." → "are referred to."

We have fixed the typo to clarify the statement.

(3) Figure 3 caption: "color scheme in the plots are same" → should be "is the same."

We have fixed the typo to clarify the statement.

(4) Clarification on reporting confidence intervals: The manuscript reports confidence intervals (CIs) for the model-based comparisons (e.g., Figures 2-3). This might seem unnecessary for simulation studies, since running more iterations can arbitrarily shrink uncertainty. However, in your case, the CIs are justified because the simulations are anchored to a finite empirical dataset (only 9 solo trajectories), sampled with replacement, and analyzed with mixed-effects models that incorporate bird identity as a random effect. Thus, the intervals reflect biological sample variability rather than simulation noise. This must be clarified.

We have added a clarifying statement: “...and reflect the biological uncertainty in the empirical dataset, not simulation noise” found in lines 241 and 293 in the captions of Figures 2 and 3 in accordance with the reviewer’s comment. 

(5) One part of the issue is that details of methods come much later in the manuscript, perhaps following journal style. Therefore, I recommend explicitly highlighting this rationale in the Results, so readers do not misinterpret the CIs as simply reflecting simulation error.

We believe that the clarifying statements we have now added in the captions of Figures 2 and 3 should convey this interpretation of CIs and further changes in the Results may not be required.

With these proposed changes we hope that we improved upon the clarity of our manuscript.

References:

(1) Dalmaijer ES (2024) Cumulative route improvements spontaneously emerge in artificial navigators even in the absence of sophisticated communication or thought. PLoS Biol. 22:e3002644.

(2) Reindl, E., Gwilliams, A.L., Dean, L.G. et al. (2020) Skills and motivations underlying children’s cumulative cultural learning: case not closed. Palgrave Commun 6, 106.

(3) Caldwell CA, Millen AE (2008) Studying cumulative cultural evolution in the laboratory. Phil. Trans. R. Soc. B 363:3529-3539.

eLife Assessment

This important manuscript reports a very interesting view of how pesticides can be toxic to beneficial insects like the honeybee. The study uses machine learning for the discovery of new honeybee-repellent odorants. The solid evidence predicts compounds that were validated in the lab and in the field. This work will be of great interest to researchers in ecology, pest control and sensory biology.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Original review:

Summary:

This manuscript reports a very interesting, novel and important research angle to add to the now enormous interest in how pesticides can be toxic to beneficial insects like the honey bee. Many studies have reported on how pesticides in standard use formulations show both lethality as well as sublethal negative effects on behavior and reproduction. The authors propose to use machine learning algorithms to identify new volatile compounds that can be tested for repellency. They use as input chemical structures that are derived from chemicals that have known repellent effects as identified in their initial behavioral assays.

Strengths:

The conclusion is that such chemicals specific to repelling bees and not pest insects (using the fruit fly as a model for the latter) can be identified using the ML approach. Have a list of such chemicals that can be rotated among in any field application would be a benefit because of the honey bees' ability to learn its way around any kind of stimulus designed to keep it from nectar and pollen, even when they may be tainted by pesticide.

Weaknesses:

The use of machine learning seems well-executed and legitimate. But this is beyond my expertise. So other reviewers can maybe comment more on that.

The behavioral data report on the use of a two-choice assay for bees in small Petrie plates. Bess can feed from two small wells place of filter paper impregnated with control or the control containing a chemical. The primary behavior, for ex in Fig 2C, is the first choice by one of the five bees in the plate of which well to feed from. For some chemical compound, there seems to be a 50:50 choice, indicating no repellent effects. In other cases the first bee making the choice chose the control, indicating possible repellent effects of the test chemical. Choices in this assay were validated in a free flying assay.

Concerns with the choice assay:

- 50-70 microliters amounts to what one hungry bee will drink. Did the first bee drink most of it, such that measures of bait consumed reflect a single bee or multiple bees?<br /> - How many bees were repelled to the control side? Was it just the one bee? Were other measures considered? E.g. time to first approach; the number of bees feeding at different time points; the total number of bees observed feeding per unit time.

Reviewer #2 (Public review):

Original review:

Summary:

The search for new repellent odors for honey bees has significant practical implications. The authors developed an iterative pipeline through machine learning to predict honey bee-repellent odors based on molecular structures. By screening a large number of candidate compounds, they identified a series of novel repellents. Behavioral tests were then conducted to validate the effectiveness of these repellents. Both the discovery and the methodological approach hold value for related fields.

Strengths:

* The study demonstrates that using molecular structures and a relatively small training dataset, the model could predict repellents with a reasonably high success rate. If the iterative approach works as described, it could benefit a wide range of olfaction-related fields.<br /> * The effectiveness of the predicted repellents was validated through both laboratory and field behavioral tests.

Weaknesses:

The small size of the training dataset poses a common challenge for machine learning applications. However, the authors did not clearly explain how their iterative approach addresses this limitation in this study. Quantitative evidence demonstrating improvements achieved in the second round of training would strengthen their claims. For instance, details on whether the success rate of predictions or the identification of higher-affinity components would be helpful. Furthermore, given that only 15 new components were added for the second round of training, it is surprising that such a small dataset could result in significant improvements.

Reviewer #3 (Public review):

Original summary:

The manuscript of Kowalewski et al. titled "Machine learning of honey bee olfactory behavior identifies repellent odorants in free flying bees in the field" did machine learning to predict potential candidates for honeybee repellents, which may keep foraging bees from pesticides. This is a pilot research with strong significance in the research of olfactory behavior and in pest control.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript reports a very interesting, novel and important research angle to add to the now enormous interest in how pesticides can be toxic to beneficial insects like the honey bee. Many studies have reported on how pesticides in standard use formulations show both lethality as well as sublethal negative effects on behavior and reproduction. The authors propose to use machine learning algorithms to identify new volatile compounds that can be tested for repellency. They use as input chemical structures that are derived from chemicals that have known repellent effects as identified in their initial behavioral assays.

Strengths:

The conclusion is that such chemicals specific to repelling bees and not pest insects (using the fruit fly as a model for the latter) can be identified using the ML approach. Have a list of such chemicals that can be rotated among in any field application would be a benefit because of the honey bees' ability to learn its way around any kind of stimulus designed to keep it from nectar and pollen, even when they may be tainted by pesticide.

Weaknesses:

The use of machine learning seems well-executed and legitimate. But this is beyond my expertise. So other reviewers can maybe comment more on that.

The behavioral data report on the use of a two-choice assay for bees in small Petrie plates. Bess can feed from two small wells place of filter paper impregnated with control or the control containing a chemical. The primary behavior, for ex in Fig 2C, is the first choice by one of the five bees in the plate of which well to feed from. For some chemical compound, there seems to be a 50:50 choice, indicating no repellent effects. In other cases the first bee making the choice chose the control, indicating possible repellent effects of the test chemical. Choices in this assay were validated in a free flying assay.

Concerns with the choice assay:

50-70 microliters amounts to what one hungry bee will drink. Did the first bee drink most of it, such that measures of bait consumed reflect a single bee or multiple bees?

The measure of lure consumed reflects multiple bees. We observed that the first bee did not empty the 70 ul of honey, allowing us to estimate honey consumption by several bees.

How many bees were repelled to the control side? Was it just the one bee?

All the bees in a group were repelled to the control side for repellents. Evaluating lack of honey consumption, also allowed us to repellency as well. As an example: if 100% honey is consumed on the control side meant that the bees were hungry, but if 0% honey was consumed on the repellent side, this meant that the bees were not hungry enough to drink from the honey on the repellent side.

Were other measures considered? E.g. time to first approach; the number of bees feeding at different time points; the total number of bees observed feeding per unit time.

Bees were cooled down to place them in the plates for the experiments. Therefore, time to first approach could also depend on how long it took the bees to warm up, which was not as relevant for our research question. Because bees can communicate where to find food sources to each other, we restricted ourselves to first choice, only, to get independent data points for each plate. However, we investigated whether the first cup the first bee chose was also the one it drank from, which was the case.

Reviewer #2 (Public review):

Summary:

The search for new repellent odors for honey bees has significant practical implications. The authors developed an iterative pipeline through machine learning to predict honey bee-repellent odors based on molecular structures. By screening a large number of candidate compounds, they identified a series of novel repellents. Behavioral tests were then conducted to validate the effectiveness of these repellents. Both the discovery and the methodological approach hold value for related fields.

Strengths:

The study demonstrates that using molecular structures and a relatively small training dataset, the model could predict repellents with a reasonably high success rate. If the iterative approach works as described, it could benefit a wide range of olfaction-related fields.

The effectiveness of the predicted repellents was validated through both laboratory and field behavioral tests.

Weaknesses:

The small size of the training dataset poses a common challenge for machine learning applications. However, the authors did not clearly explain how their iterative approach addresses this limitation in this study. Quantitative evidence demonstrating improvements achieved in the second round of training would strengthen their claims. For instance, details on whether the success rate of predictions or the identification of higher-affinity components would be helpful. Furthermore, given that only 15 new components were added for the second round of training, it is surprising that such a small dataset could result in significant improvements.

The original repellency dataset was collected from multiple older studies, each with differences in assays for bee behavior, and using differing delivery and chemical concentrations. Moreover, the number of strong repellents were limited in number, and because they varied structurally from non-repellents in the dataset, the AUC appeared high. A smaller dataset result in unusual AI/ML model performance trends, as any algorithm is just a reflection of its training data. As a result, we found that the Round 1 predictions had a low success rate in behavior assays (~20%). Subsequently, even small amounts of data collected using one standard concentration and assay, could dramatically change the quality of the dataset, not just for structures of repellents, but also related structures that were not repellent. What we observe is a more complete representation of how repellents and non-repellents are distributed when adding just 15 chemicals. And the prediction success of Round 2 is more than doubled in repellent behavior assays at >50%. The initially observed performance gains with even small additions to the training dataset will stabilize and ultimately plateau due to the limits of the ML algorithm and/or chemical featurization technique. A more complex model, trained on a large dataset, may not be expected to benefit from a handful of additional examples, it is because the chemical feature distributions are already better approximations of the real world. To put simply, smaller datasets imply there is more to learn.

It is also true that the size of the training dataset is important for AI/ML algorithms, Artificial neural network, for instance, are highly sensitive to noise and generalize poorly with limited data; the noise is amplified in these cases, and the solution—reducing the complexity of the model—impedes learning. Many algorithms like the decision trees and support vector machines featured in our paper can handle noise more efficiently and are suitable for smaller datasets in that they can still make reasonably successful predictions.

Reviewer #3 (Public review):

The manuscript of Kowalewski et al. titled "Machine learning of honey bee olfactory behavior identifies repellent odorants in free flying bees in the field" did machine learning to predict potential candidates for honeybee repellents, which may keep foraging bees from pesticides. This is a pilot research with strong significance in the research of olfactory behavior and in pest control. However, some major issues need to be addressed to enhance the manuscript's clarity, strength, and overall coherence.

(1) Drosophila melanogaster is not considered as a true agricultural pest. The manuscript would be more compelling if using true pests, for example, Drosophila suzukii or others.

Honeybees face a critical risk of lethal pesticide exposure when they drift from their designated orchards into adjacent blooming crops or honeydew-coated fields, where they encounter chemical treatments intended for insects like Citrus Thrips, Asian Citrus Psyllid, Alfalfa Weevil, Peach Twig Borer, Oriental Fruit Moth, Lygus Bugs , Cotton Aphids, Whiteflies, Corn Rootworm, Sunflower Head Moth, Vine Mealybug, Cucumber Beetles, and Sugarcane Aphids. Unfortunately, testing such pest species is outside the scope of this paper, but would deserve further research.

(2) For repellency test, the result relies on dosage. An attractant may become a repellent at high concentration. Test a range of concentrations for each chemicals and compare responses between honeybees and pests.

Testing freely flying honey bees in the field is an extremely challenging undertaking. Nevertheless, we added extra tests for two strong repellents, BR4.5 and BR3.81, at half dose of 0.05 mg/cm². As expected, we found that there was a reduction in repellency. Testing more concentrations was not within the scope of this paper.

(3) Be more clear about bee behavior data and their scores (as in Page 4 Results "184 training chemicals and later for 203 chemicals" and Page 10 Methods). I suggest that authors add a supplemental table with each chemical and its behavioral score, feature and reference - which ones were used for training, and which ones for testing. Also add your own behavioral test data (second input) to this table

We have added the training chemical lists as Supplemental Tables S3 and S4.

(4) The AUC in the first validation was 0.88 (Page 4), and in Page 5, "As expected, the computational validation results based on the AUC values, show an improvement." However, there were no other AUC values to show improvement.

(5) Show plots of ROC AUC curves from Round 1 and Round 2.

The round one ROC curve is shown in Figure 1. The round two ROC curves obtained from 3 different approaches (Author response image 1). The manuscript shows direct behavioral validation of chemicals identified, which is more important.

Author response image 1.

(6) In the Discussion, the authors mentioned olfactory receptors in honeybees. It would be useful to provide a general review of the current understanding of these receptors and their (potential) functions.

We have expanded the discussion and pointed to a review on honey bee olfaction.

(7) I suggest combining Fig. 1 and Fig. 3A as one pipeline for this work.

(8) Figure 2C, some sample sizes are very small, such as 2-piperidone: 1 first-choice control vs 0 first-choice repellent? Increase sample size and do statistical analysis.

Most compounds except the one pointed out, have small sample sizes because of the low percentage of bees participating in the trials. Consequently, we improved methods in round 2 and were able to increase participation from 68% to 81%, as described in the methods. However since the compound was included in the second round of training, we would like to report it anyway. This compound had the highest rate of non-participating plates compared to the others and there is a possibility that it it may affect both the stimuli.

(9) In general, to assist reviewers, include line numbers to the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Other factors about the newly identified chemicals:

Is there a toxicity index for these chemicals that can be listed? This would be important obviously for any humans around the repellents

While toxicity index determination is outside the scope of this manuscript, it is possible to predict Rat LD50 values using the EPA Suite’s toxicity prediction tool. In a pilot test, the software predicted an average oral toxicity is ~3064mg/kg for the 18 repellents in Round 2, which is considered “Practically non-toxic” by the EPA.

Was there any indication of bees being behaviorally impaired or dying when exposed to the chemicals in a confined space? Even exposure to intense floral perfumes in a confined space and be toxic over a longer period.

Less than 5% of the 2225 honey bee died after the experiments, and none of the compounds showed a significantly higher level of dying, suggesting that the minor effect was not due to chemicals, but possibly due to handling steps (starving, chilling, recovery, etc).

The 'plates not participating' measure indicates plates in which no bees fed on either choice. Is that correlated to the choice index? That is, when bees showed some repellency was it the case that often that led to no choice?

Yes, non-participating plates were those, in which the bees did not drink any honey at all. The reason for this could have been that the bees were too cold and unable to heat up enough to participate in the trials, or that the chemical was so repellent, the bees did not want to drink any honey at all. Because we were not able to distinguish between these two reasons, we excluded plates in which the bees did not drink any honey at all from our dataset.

It is unclear why the McNemar test was used.

The McNemar test is used for hypothesis testing for paired dichotomous data. In our data file, we created two columns to report our first-choice results: “Control side first” and “Repellent side first”. When the first bee in a plate drank from the control side first, we added a 1 to the “Control side first” column and a “0” to the “Repellent side first” column. Because one control and one repellent-side honey pot were in the same Petri dish, the bees could only choose one side first, this meant it could not choose the other side at the same time. Consequently, our dataset consisted of paired samples, which were dependent from each other. We therefore split the dataset by Repellent candidate, and we used the paired -sample McNemar tests for non-parametric data. (Lachenbruch P.A. McNemar Test, Wiley StatsRef: Statistics Reference Online)

The statistical result is not discussed in the text, only shown in the figure. And it looks to be significant only for one chemical and DEET. Yet on page 4 the end of the second paragraph, the authors write "For many of the tested compounds the bees preferred to visit the honey-water pots on the control side versus the repellent side,". That implies that they are not really using the test as a meaningful means for showing differences. If they are arguing only from trends, then that should be clearer in the text.

We reported the p-values for each test we had used in tables in Figure 2C and S2. In the methods section we report which statistical tests were used to evaluate the data.

There is no mention of attractant chemicals:

Slessor and Winston used queen pheromone to attract bees to fields and improve pollination. Honey bees use the Nasonov pheromone to attract other bees to feeding locations. Could the addition of their chemical features change ML outcomes? This should be at least discussed.

We thank the referee for the suggestion; however the focus this manuscript is repellents and therefore we restricted the background to that area of knowledge.

Reviewer #2 (Recommendations for the authors):

Minor comments:

Releasing the dataset and code will benefit the readers interested in this study.

The behavioral data are reported within the figures, tables, and supplementary. The computational code will be available upon request from the communicating author for non-commercial use.

Figure 1, AUC curve, "AUC = 0.XX", should there be an actual value from the experiment?

Added

Page 4, "(Talbe S1)" should be placed in the next sentence, as "From the initial training set we identified 45 features that were considered important for predicting aversive valence (Table S1)."

We have added this in the appropriate spot.

Page 5, "As expected, the computational validation results based on the AUC values, show an improvement.". Please list the AUC values.

Author response image 2.

Reviewer #3 (Recommendations for the authors):

Minor comments:

(1) Page 3: "they sense using a sophisticated olfactory system of >180 odorant receptor genes in the genome". In the cited Robertson & Wanner's paper, there are around 160 receptors, and 170 if pseudogenes are included.

We thank the referee and have updated the numbers.

(2) Page 4: "initially for 184 training chemicals and later for 203 chemicals (Table S1)." Table S1 is about features, not chemicals?

We have moved the reference to an appropriate location.

(3) Figure 2A: What is the control? Acetone or another solvent?

Acetone, but it rapidly evaporates before the time of experiment.

(4) Figure 2A: What does asterisks mean?

Statistically significant.

(5) Figure 3: When you added your own testing data as a second input for Round 2, put details about these data: chemical names, preference scores... Also, are Round 2 data (Round 1 plus your own) were also split as 90:10 into training and testing partitions?

Yes, the validation was performed on the updated data set including the new chemicals.

(6) Figure 3D: Is asterisk at correct location? What does it mean?

Means that BR3.15 was significantly different from BR4.5

(7) Figure 4D: "4D" in legend is missing. Also, "... tested at the regular dose (0.1mg/cm2) and half dose (0.05mg/cm2)". In the panel, it is only 0.05mg/cm2.

Added

(8) Table S2 is the same as Fig. 2C? Remove one.

We have deleted Table S2.

eLife Assessment

This meta-analysis provides a fundamental synthesis of evidence demonstrating that transcranial magnetic stimulation targeting the hippocampal-cortical network reliably enhances episodic memory performance across diverse study designs. The evidence is convincing, with rigorous methodology and consistent effects observed despite modest sample sizes and some heterogeneity in stimulation approaches. The work highlights the specificity of memory improvements to hippocampal-dependent memories and identifies key methodological factors-such as individualized targeting-that influence efficacy. Overall, this study offers a timely and integrative framework that will inform both basic memory research and the design of future clinical trials for cognitive enhancement.

Reviewer #1 (Public review):

Summary:

Goicoechea et al. conducted a timely and thorough meta-analysis on the potential for indirect hippocampal targeted transcranial magnetic stimulation (TMS) to improve episodic memory. The authors included additional factors of interest in their meta-analysis which can be used to inform the next generation of studies using this intervention. Their analysis revealed critical factors for consideration: TMS should be applied pre-encoding, individualized spatial targeting improves efficacy, and improvement of recollection was stronger than recognition.

Strengths:

As mentioned previously, the meta-analysis is timely and summarizes an emerging set of studies (over the past decade since Wang et al., Science 2014). Those outside of the field may not be aware of the robustness in improvements in episodic memory from hippocampal targeted TMS. The authors were quite thorough in including additional factors which are important for the interpretation of these findings. These factors also address the differences in approach across studies. The evidence that individualized spatial targeting improves TMS efficacy is consistent with recent advances in TMS for major depressive disorder. The specificity of the cognitive improvements to recollection of episodic memory and not for other cognitive domains is consistent with hippocampal targeting. The authors also plan to post the complete dataset on an open-source repository which enables additional analysis by other researchers.

Weaknesses:

The write-up is succinct and emphasizes the scientific decisions that underly key differences in the various experimental designs. While the manuscript is written for a scientific audience, the authors are likely aware that findings like this will be of broad appeal to the field of neurology where treatments for memory loss are desperately needed. For this reason, the authors could consider including a statement regarding an interpretation of this meta-analysis from a clinical standpoint. Statements such as 'safe and effective' imply a clinical indication and yet the manuscript does not engage with clinical trials terminology such as blinding, parallel arm versus crossover design, and trial phase. While the authors might prefer not to engage with this terminology, it can be confusing when studies delivering intervention-like five-days of consecutive TMS (e.g., Wang et al., 2014) are clustered with studies that delivered online rhythmic TMS which tests target engagement (e.g., Hermiller et al., 2020). While the 'sessions' variable somewhat addresses the basic-science versus intervention-like approach, adding an explicit statement regarding this in the discussion might help the reader to navigate the broad scope of approaches that are utilized in the meta-analysis.

Following revision: The authors have adequately addressed my concerns.

Reviewer #2 (Public review):

Parietal lobe TMS, targeted to the episodic memory network via connections with the structures in the medial temporal lobe, improves episodic memory. This is one of very few robustly reproduced cognitive findings in noninvasive brain stimulation. The comprehensive review and detailed meta-analysis by Goicoechea et al. makes a convincing case for efficacy in healthy people and will be important for neuroscientists and clinical researchers in memory and dementia.

In 2014, Wang et al. showed that noninvasive stimulation of a parietal site, connected functionally to the hippocampus, increased resting state functional connectivity throughout a canonical network associated with episodic memory. It also caused a memory boost which was proportional to the connectivity increase within subjects. Their discovery that an imaging biomarker could (1) be used to target a functional network with critical nodes too deep to reach directly with TMS, (2) enable individualized, functionally confirmed, targeting, and (3) provide a scaling measure of target engagement, is one of the signal advances in noninvasive brain stimulation.

The meta-analytical methodology used by these authors is rigorous, and the central finding, viz. that high-frequency, network-targeted stimulation reproducibly improves event recall, is amply supported. The question of whether to stimulate before or after memory encoding is also answered. While there is a hint that individualized anatomical or functional MRI-based targeting may be superior to atlas or group average-based techniques, the finding did not survive correction for multiple comparisons. Additional studies will be needed to resolve this issue, optimize the stimulation delivery parameters, and further define the behavioral effect.

While the authors appropriately emphasize the associated network rather than the hippocampus itself, naming the target after a single node could suggest a primary role for the hippocampus in the observed outcomes, a conclusion not supported by the data reviewed here. Other nodes in the network are be equally important to aspects of episodic memory and could be useful targets for stimulation.

Despite encouraging results from small clinical samples, the question of efficacy in patients with static lesions and ongoing neurodegeneration remains open. The information gathered here, including the absence of reported adverse events, should spur Phase 2 clinical trials in patients with disorders of memory.

Reviewer #3 (Public review):

Summary:

The manuscript by Goicoechea et al. assesses the influence of hippocampal-network targeted TMS to parietal cortex on episodic memory using a meta-analytic approach. This is an important contribution to the literature, as the number of studies using this approach to modulate memory/hippocampal function has clearly increased since the initial publication by Wang et al. 2014. This manuscript makes an important contribution to the literature. In general, the analysis is straightforward and the conclusions are well-supported by the results.

Strengths:

(1) A meta-analysis across published work is used to evaluate the influence of hippocampal-network-targeted TMS in parietal cortex on episodic memory. By pooling results across studies, the meta-analytic effects demonstrate an influence of TMS on memory across the diversity of many details in study design (specific tasks, stimuli, TMS protocols, study populations).

(2) Selectivity with regard to episodic memory vs. non-episodic memory tasks is evaluated directly in the meta-analysis.

(3) The investigation into supplemental factors as predictors of TMS's influence on memory was tested. This is helpful given the diversity of study designs in the literature. This analysis helps to shed light on which study designs, e.g., TMS protocols, etc., are most effective in memory modulation.

Weaknesses:

The authors thoroughly addressed and responded to the prior comments in the revision. The only minor weakness I see is acknowledged in terms of how null effects for particular design or TMS features should be interpreted (i.e., with caution given the regression approach used).

Author response:

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

Reviewer #1 (Public review):

(1) While the manuscript is written for a scientific audience, the authors are likely aware that findings like this will be of broad appeal to the field of neurology, where treatments for memory loss are desperately needed. For this reason, the authors could consider including a statement regarding an interpretation of this meta-analysis from a clinical standpoint. Statements such as 'safe and effective' imply a clinical indication, and yet the manuscript does not engage with clinical trials terminology such as blinding, parallel arm versus crossover design, and trial phase. While the authors might prefer not to engage with this terminology, it can be confusing when studies delivering intervention-like five days of consecutive TMS (e.g., Wang et al., 2014) are clustered with studies that delivered online rhythmic TMS, which tests target engagement (e.g., Hermiller et al., 2020). While the 'sessions' variable somewhat addresses the basic-science versus intervention-like approach, adding an explicit statement regarding this in the discussion might help the reader navigate the broad scope of approaches that are utilized in the meta-analysis.

We appreciate the suggestion to enhance interpretability of our report by broader audiences. First, to avoid confusion, we have eliminated “safe” and “effective” descriptors from the main summary of findings in the Abstract (pg. 1) and Discussion (pg. 6). Second, we now describe that reviewed studies included those categorized as traditional clinical trials, as well as non-clinical studies that generally follow clinical trial designs (i.e., multi-day intervention-like studies), in addition to more basic-oriented studies that are geared towards target engagement (Introduction, pg. 2). Third, we now clarify that the Design and Control factors (Figure 3) correspond to fairly standard distinctions in the clinical trials literature and were intended to capture major study design factors choices that are used in both clinical-trial and non-trial studies (Methods, pg. 9; Table S1). Finally, we now clarify that future clinical trials would be needed to evaluate HITS for any specific indication, and that our findings motivate such investigations but do not conclusively indicate efficacy for any given indication (Abstract, pg. 1; Discussion, pg. 7).

Reviewer #1 (Recommendations for the authors):

(1) The color scheme of Figure 1 was a bit confusing. All of the colors used for the flagged regions were incredibly similar. At first glance, it looks like the hippocampus was targeted directly due to the subtle color difference. Could the authors use colors that are more different? Similarly, zooming into the specific locations shows blue dots encompassed by teal. I am not sure what I am looking at here.

We have updated the figure for clarity.

(2) Given the broad appeal of the current study, I would encourage the authors to include a brief visual depiction of "HITS." This could help the more casual reader to understand the general approach.

We have included this in Figure 1A.

Reviewer #2 (Public review):

(1) While the introduction centers on the role of the hippocampus in episodic memory and posits hippocampal neuromodulation by TMS as causative, the true mechanism may be more complex. Clean hippocampal lesions in primates cause focal loss of spatial and place memory, and I am aware of no specific evidence that the hippocampus does more than this in humans. Moreover, there is evidence that lateral parietal TMS also reaches neighboring temporal lobe regions, which contribute to episodic memory. The hippocampus may, therefore, be a reliable deep seed for connectivity-based targeting of the episodic memory network, but might not be the true or only functional target.

We regret to have implied that we think the hippocampus is the true or only functional target. We agree with the reviewer that the hippocampus is “a reliable deep seed for connectivity-based targeting of the episodic memory network” and that the specific locus/loci of the HITS effects and mechanisms are not yet clear. We now emphasize that although hippocampus is used to define the targeted network, effects of TMS are likely distributed throughout the network, citing relevant studies that have shown that brain activity changes due to HITS are certainly not restricted to the hippocampus (Introduction, pg. 2).

(2) The meta-analysis combines studies with confirmation of targeting and target-network engagement from fMRI and studies without independent evidence of having stimulated the putative target (e.g., Koch et al). That seems like a more important methodological distinction than merely the use of any individual targeting method. In my experience, atlas-based estimates are at least as accurate as eyeballing cortical areas in individuals. Hence, entering individual functional targeting as a factor might reveal an effect on efficacy.

Our current definition of the “Targeting” factor appears to satisfy this concern. That is, we distinguish studies that used “individual functional targeting” (i.e., resting-state fMRI or DTI connectivity in each individual to select the target) from those that did not (i.e., atlas or other group-average approach). Notably, the Targeting factor modulation effect failed to survive correction for multiple comparisons. We think this satisfies the reviewer criticism, unless the reviewer is suggesting that we categorize studies based on whether they included evaluation of target engagement (e.g., tested for change in fMRI activity or connectivity of the network due to HITS) versus those that measured only behavioral outcomes. We did not include this distinction as a factor, as our analysis focuses on behavioral effects of HITS, and it is not clear what the neural effects would have been in studies in which they were not measured. Notably, we are providing the full raw dataset of effect sizes in a public repository with our final version of record, such that any other categorization schemes could be assessed by others.

(3) The funnel plot and Egger's regression for episodic memory outcomes suggested possible bias, and the average sample size of 23 is small, contributing to the likelihood of false positive results. It would be informative, therefore, to know how many or which studies had formal power estimates and what the predicted effect sizes were.

Regarding the average sample size of 23, we note that we used Hedges’ g for the effect size measure because it corrects for bias associated with small samples (pg. 10). Further, small sample sizes contribute to noisy estimates of true effects, allowing outliers to contribute to false positives and low power to contribute to false negatives, but without any reason to systematically yield bias towards false positives. Regarding potential publication bias, although we cannot rule this out based only on the statistics, we think that bias against publication of negative results is unlikely. First, HITS experiments are time consuming and expensive, and most in the field seem to be motivated to publish, whatever the outcome. Second, the notion of memory enhancement via brain stimulation is controversial, and groups have certainly been motivated, if not overly eager, to publish “failure to replicate” studies for HITS (e.g., the failure-to-replicate publication by Hendrikse et al. 2020, which was then re-analyzed by many of the original authors to arrive at different conclusions in Cash et al. 2022). Given these considerations, we think that it is very unlikely that publication bias had any major impact on our conclusions, but of course it cannot be conclusively excluded. Finally, we note that our finding of HITS selectivity for recollection enhancement is likely not affected by publication bias, as this selectivity versus other memory and non-memory outcomes was found only within published studies (i.e., it is very unlikely that publication bias would have led researchers to withhold publication of studies that found effects of HITS on recognition but not on recollection).

(4) In the Discussion, the authors might provide a comparison between the effect size for memory improvement found here with those reported for other brain-targeted interventions and behavioral strategies. It may also be worthwhile pointing out that HITS/memory is one of the very few, or perhaps the only, neuromodulatory effects on cognition that has been extensively reproduced and survived rigorous meta-analysis.

We now emphasize that this is, to our knowledge, the only neuromodulatory effect on cognition that is selective, has been extensively reproduced, and survived rigorous meta-analysis (Discussion, pg. 6). However, we wish to avoid the clinical overinterpretation of our findings that might result if we were to compare directly to effect size estimates for other current therapies, which have been evaluated for specific clinical indications. For example, antibody and pharmacological interventions for Alzheimer’s dementia typically have been associated with similar effect sizes to our estimate for HITS. However, those estimates derive from systematic review of randomized controlled trials measuring clinically relevant outcomes at relatively long delays, whereas the HITS studies we review include a mix of controlled and uncontrolled trials, vary in whether clinical outcomes were assessed, and mostly assessed outcomes at shorter delays. Thus, it could be misleading to directly compare the effect sizes. We instead continue to highlight that the HITS effects are promising and warrant rigorous testing for any given clinical indication.

(5) The section of the Discussion on specificity compares HITS to transcranial electrical stimulation without specifying an anatomical target or intended outcome. A better contrast might be the enormous variety of cognitive and emotional effects claimed for TMS of the dorsolateral prefrontal cortex.

We now also note that TMS of lateral frontal cortex has not been associated with similarly high specificity (Discussion, pg. 6). Note however that we cannot exclude anti-depressant or other psychological effects of HITS, as such outcomes were not consistently assessed in HITS studies and so were not included in our analyses.

(6) With reference to why other nodes in the episodic memory network have not been tested, current flow modeling shows TMS of the medial prefrontal cortex is unlikely to be achievable without stronger stimulation of the convexity under the coil, in addition to being uncomfortable. The lateral temporal lobe has been stimulated without undue discomfort.

We now additionally indicate that medial prefrontal stimulation may be ineffective given conventional TMS (Discussion, pg. 7). However, we are aware of no studies that have stimulated the portion of middle temporal gyrus that shows strong connectivity with hippocampus. We have tried this location, which positions the coil on or slightly above the ear and bordering on the temple area that is very sensitive to most. We were not able to minimize pain/discomfort for most subjects in pilot experiments, and so had to abandon it. Perhaps others have succeeded? If the reviewer has any specific references that could be included we would be happy to add them and update this section accordingly.

(7) Finally, a critical question hanging over the clinical applicability of HITS and other neuromodulation techniques is how well they will work on a damaged substrate. Functional and/or anatomical imaging might answer this question and help screen for likely responders. The authors' opinion on this would be informative.

We appreciate this point but don’t think there are enough data to assess the level of substrate damage needed to frustrate any stimulation benefits. The only thing we can say is that HITS was equally effective for mild to moderate Alzheimer’s dementia as it was for other non-neurodegenerative groups (nonsignificant effect of the Population factor, Figure 3B), suggesting that whatever degree of damage present in that group is insufficient to prevent the stimulation effects. We now highlight this point and raise the issue that, presumably, some level of damage would render HITS ineffective (Discussion, pg. 8).

Reviewer #3 (Public review):

(1) My only significant concern is how studies are categorized in the 'Timing' factor (when stimulation is applied). Currently, protocols in which TMS is administered across days are categorized as 'pre-encoding' in the Timing factor. This has the potential to be misleading and may lead to inaccurate conclusions. When TMS is administered across multiple days, followed by memory encoding and retrieval (often on a subsequent day), it is not possible to attribute the influence of TMS to a specific memory phase (i.e., encoding or retrieval) per se. Thus, labeling multi-day TMS studies as 'pre-encoding' may be misleading to readers, as it may imply that the influence of TMS is due to modulation of encoding mechanisms per se, which cannot be concluded. For example, multi-day TMS protocols could be labeled as 'pre-retrieval' and be similarly accurate. This approach also pools results from TMS protocols with temporal specificity (i.e., those applied immediately during encoding and not on board during memory testing) and without temporal specificity (i.e., the case of multi-day TMS) regarding TMS timing. Given the variety of paradigms employed in the literature, and to maximize the utility/accuracy of this analysis, one suggestion is to modify the categories within the Timing factor, e.g., using labels like 'Temporally-Specific' and 'Temporally Non-specific'. The 'Temporally-Specific' category could be subdivided based on the specific memory process affected: 'encoding', 'retrieval', or 'consolidation' (if possible). I think this would improve the accuracy of the approach and help to reach more meaningful conclusions, given the variety of protocols employed in the literature.

We agree in principle with this criticism and think that the most straightforward way to address it is to relabel the “Pre-Encoding” category as “Pre-Task”. The issue with labeling/considering single-session stimulation delivered immediately before encoding as “Pre-encoding” is that this makes the assumption that this stimulation doesn’t also affect retrieval (i.e., is temporally specific). We do not have certainty about the timecourse of how a single session of stimulation affects brain activity. We think the “Pre-Task” label and interpretation is the best way to address this, to avoid suggesting that we are confident about the timecourse/selectivity of stimulation effects. Notably, the “Sessions” factor directly compares among designs that delivered stimulation in a single session versus in multiple consecutive sessions, and was a nonsignificant modulator. Thus, our analyses already compare studies that are relatively temporally specific versus those that, likely, are less so. In addition to relabeling, we have also added clear caveats to address the interpretive constraint imposed by the unknown timecourse of stimulation effects (Discussion, pg. 6-7) and revised the Abstract to reflect this change.

(2) As the scope of the meta-analysis is limited to TMS applied to parietal or superior occipital cortex, it is important to highlight this in the Introduction/Abstract. The 'HITS' terminology suggests a general approach that would not necessarily be restricted to parietal/nearby cortical sites.

This was previously highlighted only in the Methods and Discussion (with a Discussion paragraph dedicated to the issue of target selection; see also Comment 6 from Reviewer 2). We now also note this in the Introduction (pg. 2) and Abstract.

Minor:

(1) To reduce the number of study factors tested, data reduction was performed via Lasso regression to remove factors that were not unique predictors of the influence of TMS on memory. This approach is reasonable; however, one limitation is that factors strongly correlated with others (and predict less unique variance) will be dropped. This may result in a misrepresentation, i.e., if readers interpret factors left out of this analysis as not being strongly related to the influence of TMS on memory. I do see and appreciate the paragraph in the Discussion which appropriately addresses this issue. However, it may be worth also considering an alternative analysis approach, if the authors have not already done so, which explicitly captures the correlation structure in the data (i.e., shown in Figure S2) using a tool like PCA or an appropriate factor analysis. Then, this shared covariance amongst factors can be tested as predictors of the influence of TMS - e.g., by testing whether component scores for dominant PCs are indeed predictive of the influence of TMS. This complementary approach would capture rather than obfuscate the extent to which different factors are correlated and assess their joint (rather than independent) influence on memory, potentially resulting in more descriptive conclusions. For example, TMS intensity and protocol may jointly influence memory.

We argue that feature selection via Lasso regression is a better approach for our research question than PCA, factor analysis, or other latent variable methods. The main reason is that PCA would sacrifice the interpretability of our findings with respect to the design of future experiments using or testing HITS. That is, because PCA creates composite components that are linear combinations of multiple variables, we would lose the ability to provide clear, actionable guidance to researchers about which specific study design choices (e.g., stimulation intensity, protocol type, timing) influence memory outcomes. Given that a major goal of our meta-analysis is to inform future experimental design, we believe that it is essential to maintain interpretability of the individual factors that must be decided when designing a study. Regarding factor analysis, this approach would require making a priori theoretical decisions about how to group individual moderators, which could introduce subjective bias into the analysis and would introduce other complications such as a need for validation of the resulting factor scores. We believe that the exploratory nature of our investigation, examining which among many possible study design factors substantially determine TMS efficacy, is better suited to a data-driven selection approach like Lasso. While the reviewer correctly notes that Lasso may drop factors that are correlated with stronger predictors, this feature can be considered advantageous in terms of identifying factors for inclusion in future study designs. That is, this can help identify the most parsimonious set of independent predictors, such that researchers can focus on the study design elements that matter most when controlling for other factors. Notably, we provide the table of factor relationships (Figure S2) so that interested readers can inspect how dropped factors were related to those that were retained.

It is also important to note that we have provided the full dataset with our resubmission, which has been deposited in Dryad with a link in the Data Availability section (pg. 15). Thus, others are free to explore alternative analytical approaches should they wish to examine the data from different perspectives or to answer different questions.

(2) Given the specific focus on TMS applied to parietal cortex to modulate hippocampal and related network function, it would be fruitful if the authors could consider adding discussion/speculation regarding whether this approach may be effectively broadened using other stimulation methods (e.g., tACS, tDCS), how it may compare to other non-invasive brain stimulation methods with depth penetration to target hippocampal function directly (transcranial temporal interference, or transcranial focused ultrasound), and/or how or whether other stimulation sites may or may not be effective.

We briefly discuss a meta-analysis of tACS studies which reported nonspecific effects, including for parietal targets overlapping those used for HITS (Discussion, pg 6). We briefly speculate about how tES effects remain mechanistically uncertain. We are afraid that further speculation about other stimulation modalities and targets would be beyond the scope of this focused meta-analysis, given especially the few datapoints for newer approaches such as TI or tFUS.

(3) Studies were only included in the meta-analysis if they contained objective episodic memory tests. How were studies handled that included both objective and subjective memory, or other non-episodic memory measures? For example, Yazar et al. 2014 showed no influence of TMS on objective recall, but an impairment in subjective confidence. I assume confidence was not included in the meta-analysis. Similarly, Webler et al. 2024 report results from both the mnemonic similarity task (presumably included) and a fear conditioning paradigm (presumably excluded). Please clarify in the methods how these distinctions were handled.

Studies were included in our meta-analysis if they included at least one objectively scorable test of episodic memory. We only included objectively scorable test performance in our analysis, excluding scores from any other subjective measures if they were also reported. This is now clarified in Methods (pg. 9).

(4) The analysis comparing memory to non-memory measures is important, showing the specificity of stimulation. Did the authors consider further categorizing the non-memory tasks into distinct domains (i.e., language, working memory, etc.)? If possible, this could provide a finer detail regarding the selectivity of influences on memory vs. other aspects of cognition. It is likely that other aspects of cognition dependent on hippocampal function may be modulated as well, i.e., tasks with high relational/associative processing demands.

This is an interesting idea, but it is beyond our expertise to categorize these other tasks based on the nature of processing demands that they capture. Note that the task names are provided in the data table that we are making available online with our submission of record (via Dryad), such that other groups could address this question if interested.

(5) In the analysis of the Intensity factor, how were studies using Active (rather than resting) MT categorized? Only resting MT is mentioned in Table S1. This is important as the original theta-burst TMS protocol from Huang et al. 2005 determines intensity based on Active Motor Threshold.

MT was resting/passive in all reviewed studies except for one (Tambini et al. 2018), which used 80% of active MT. We categorized this as <100% MT for the Intensity factor, as it was <100% of MT as defined in that study. Although one could make the argument that 80% AMT might instead correspond to 100+% RMT, this change would have very little influence on our results or conclusions. We now clarify this in Table S1.

(6) Is there a reason why the study by Koen et al. 2018 (Cognitive Neuroscience) was not included? TMS was performed during encoding to the left AG, and objective memory was assessed, so it would seemingly meet the inclusion criterion.

The failure to include Koen et al. 2018 was our error. Koen et al. 2018 is the only study that used “online” stimulation, delivered during the trials when memoranda were displayed for encoding in the task. In contrast, all other reviewed studies delivered “offline” stimulation either before the memoranda was presented (“Pre-Task”) or after the encoding period but before retrieval (“Post-Encoding”). Therefore, categorization for the “Timing” factor would be problematic for its inclusion in the main analysis. We therefore now include Koen et al. 2018 in the “Supplementary Results” section as well as the corresponding main Results section on “Similar outcomes in studies that were excluded from meta-analysis”. We also note in the relevant discussion that “online” stimulation, as done in Koen et al. 2018, is typically considered disruptive (e.g., Beynel et al. 2019 Neuroscience & Biobehavioral Reviews; Yeh & Rose 2019 Frontiers in Psychology), which should be taken into account when considering the findings of Koen et al. 2018 relative to other reviewed studies that used “offline” designs.

(7) It would be helpful to briefly differentiate the current meta-analysis from that performed by Yeh & Rose (How can transcranial magnetic stimulation be used to modulate episodic memory?: A systematic review and meta-analysis, 2019, Frontiers in Psychology) (other than being more current).

Beyond being more current and therefore including many more studies in which stimulation targets were based on hippocampal connectivity (which tend to have been published more recently), the differences with Yeh & Rose 2019 are subtle. Our review focuses on assessment of network targeting and whether effects were specific to episodic memory versus other tasks, which differs somewhat from the focus of Yeh & Rose 2019. The main difference in conclusions likely derives from there being more network-focused memory TMS experiments now than were available for Yeh & Rose’s review. We also differentiate episodic memory into recollection versus other components to test specificity and analyze modulation by many study design factors relevant to HITS studies that were not emphasized in Yeh & Rose’s review. Note that we now cite Yeh & Rose for those interested in potential differences.

(8) For transparency and to facilitate further understanding of the literature and potential data re-use, it would be great if the authors consider sharing a supplementary table or file that describes how individual studies/memory measures were categorized under the factors listed in Table S1.

As promised in our original submission, we are providing the full data table, including how individual studies and memory measures were categorized, as an open dataset in Dryad. The Dryad dataset is cited in “Data availability” (pg. 15).

Reviewer #3 (Recommendations for the authors):

Please explicitly state in the Methods (Meta-analysis of effect modifiers section) that the criteria used for categorizing each measure into a factor (e.g., probing Recollection, Recognition, etc.) are fully described in Table S1; this will help readers to find these details (it took me a while!).

This is now emphasized (pg. 10).

eLife Assessment

In this important study, the authors conducted atomistic molecular dynamics simulations to probe the interactions between IRE and unfolded peptides. The results help reconcile contradicting experimental findings in the literature and offer mechanistic insights into the activation of the unfolded protein response. The atomistic molecular dynamics simulations performed are solid, leading to convincing conclusions that are partly supported by experimental validations. The use of unbiased molecular dynamics simulations, while appropriate for the current system due to its complexity, limits the time scale of events that can be observed and therefore the proposed mechanism of recognition merits further confirmation by future studies.

Reviewer #1 (Public review):

Summary:

This work provides structural and mechanistic insights into the disordered protein recognition process inside the endoplasmic reticulum by the inositol-requiring enzyme 1. Using state-of-the-art molecular dynamics simulation tools, the authors propose a mechanism of disordered protein recognition that reconciles contradictory findings of biochemical and structural biology experiments.

Strengths:

(1) All MD simulations have been carried out in triplicates, and several different folded conformations were generated using alphafold2. This provides adequate statistics to draw meaningful conclusions from the simulations.

(2) Potential limitations of the disordered protein force fields and water models have been taken into consideration. Particularly, performing the simulation in both TIP3P and TIP4PD water models ensures that the conclusions drawn are not influenced by the force field choice.

(3) The binding of a large number of disordered peptides was investigated, ensuring that the conclusions drawn about disordered peptide recognition are sufficiently general.

Weaknesses:

(1) The timescales of the peptide recognition and unbinding process are much longer than what can be sampled from unbiased simulations. Therefore, the proposed mechanism of recognition should only be considered a hypothesis based on the results presented here. For example, peptides that do not dissociate within one microsecond MD simulation are considered to be stable binders. However, they may not have a viable way to bind to the narrow protein cleft in the first place.

(2) Oftentimes, representative structures sampled from MD simulation are used to draw conclusions (e.g., Figure 4 about the role of R161 mutation in binding affinity). This is not appropriate as one unbinding event being observed or not observed in a microsecond-long trajectory does not provide sufficient information about the binding strength of free energy difference.

Comments on revisions:

The authors have adequately addressed my comments. I have no further comments.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors investigated the interactions between IRE and unfolded peptides using all-atom molecular dynamics simulations. The interactions between a couple of unfolded peptides and IRE provide mechanistic insight on the activation of the UPR.

Strengths:

- Well-written manuscript accessible for a broad biological audience

- State-of-art structural predictions and all-atom simulations

- Validation with existing experimental data<br /> - Clear schematic diagram summarizing mechanisms learned from simulations

- Error estimate included

- Shared simulation data and code in public repository

Weakness:

No major concerns remain after revision.

Comments on revisions:

The authors have addressed all my questions from the previous assessment. I do not have more suggestions.

Reviewer #3 (Public review):

Summary:

In this important work, the authors use extensive MD simulations to study how the IRE1 protein can detect unfolded peptides. Their study consolidates contradictory experimental results and offers a unique view of the different sensing models proposed in the literature. Overall, it is an excellent study that is quite extensive. The research is solid, meticulous, and carefully performed, leading to convincing conclusions.

Strengths:

The strength of this work is the extensive and meticulous molecular dynamics simulations. The authors use and investigate different structural models, for example carefully comparing a model based a PDB structure with reconstructed loops with a AlphaFold 2 Multimer model. The authors also investigate a wide range of different protein structural models that probe different aspects of the peptide-sensing process. Additionally, the authors experimentally validate a part of the simulation results. These solid and meticulous MD simulations allow the authors to obtain convincing conclusions concerning the peptide-sensing process of the IRE1 protein.

Weaknesses:

A potential weakness of the study is the use of equilibrium (unbiased) molecular dynamics simulations, which means only processes and conformational changes on the microsecond timescale can be probed. Furthermore, there can be inaccuracies and biases in the description of unfolded peptides and protein segments due to the protein force fields. Here, it should be noted that the authors do acknowledge these possible limitations of their study in the conclusions. Furthermore, in the revised version, the authors partly address this weakness by employing orthogonal simulation methods and experimental techniques.

Comments on revisions:

The authors have addressed all the issues that I raised in my previous report.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer 1 (Public review):

(1) "The timescales of the peptide recognition and unbinding process are much longer than what can be sampled from unbiased simulations. Therefore, the proposed mechanism of recognition should only be considered a hypothesis based on the results presented here. For example, peptides that do not dissociate within one one-microsecond MD simulation are considered to be stable binders. However, they may not have a viable way to bind to the narrow protein cleft in the first place."

We thank the Reviewer for this valuable feedback and we agree with the Reviewer. Our work on the IRE1 cLD activation mechanism is focused on generating a hypothesis of the binding mechanism driven by MD simulations. We recognize the limitations in defining a stable binder due to the time scales sampled. However, our primary focus was to sample and characterize a possible binding pose in the center of the cLD dimer. We contextualized our statements about stable binders and limited our claims to stating that the protein-peptide complex is stable within 1 µs-long simulations. However, we believe that our finding that the cLD dimer groove is not able to accommodate peptides is solid, as the steric impediment described is present in all our replicas, both with and without peptides, in a cumulative sampling time of 24 µs without peptides and 66 µs with peptides. Additionally, we included a plot showing the distribution of groove width across all replicas.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) The title was changed from “Unfolded polypeptides can stably bind to hIRE1α cLD dimer” to “Unfolded polypeptides bind to hIRE1α cLD dimer surface”

Addition to the text. (Figure 15 A legend) “(A) Distributions of the groove width of peptide-bound cLD dimers throughout all simulations performed. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(2) Oftentimes, representative structures sampled from MD simulation are used to draw conclusions (e.g., Figure 4 about the role of R161 mutation in binding affinity). This is not appropriate as one unbinding event being observed or not observed in a microsecond-long trajectory does not provide sufficient information about the binding strength of the free energy difference.

We thank the Reviewer for the insightful comment. As explained in the previous point, we believe that our simulations provide useful hypotheses. We are aware of the limitations due to the timescale and agree that these limitations cannot be overcome with standard equilibrium simulations. To address these limitations, used orthogonal methods, specifically MM/PB(GB)SA calculations, to calculate binding free energies from existing trajectories. We added predictions of all the peptides using AlphaFold 3, to confirm the binding region. Importantly, we now provide experimental results to assess the binding affinity of cLD dimer mutants E102R and Y161R.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. 16A). We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Figure 16 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT). (B) Difference in enthalpy (enthalpy of binding, ∆H) as an estimate of the binding free energies of unfolded polypeptides to hIRE1α cLD dimer derived from MM/PBSA calculations of our peptide simulations.”

Addition to the text. (Figure 4 G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Results section: Point mutations destabilize unfolded peptide binding to cLD) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102 K_1/2= 6.35 µM and Y161R K_1/2= 5.4 µM, Supplementary Table 3) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 3), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4G legend) “(G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary Table 3)

Reviewer 2 (Public review):

(1) Improving presentation to include more computational details.

We thank the Reviewer for raising this critical point. We agree that the manuscript is tailored for a biology audience, as the data are particularly relevant for that community. Nevertheless, we also understand the importance of providing sufficient methodological detail for computational readers. We added more references to the methods for computational information in the main text.

(2) More quantitative analysis in addition to visual structures.

We added an uncertainty estimate for the HDX calculations using bootstrapping and included additional information on bond distances for E102 and Y161. We also incorporated time-series data showing the distance of the peptide from the groove across all replicas.

Addition to the text. (Figure 1C legend) “(C) The deuterated fraction obtained from experimental results (dashed line, shaded area indicates the error we calculated from bootstrapping) published by Amin-Wetzel et al. and the fraction computed from MD simulations (solid lines, blue for TIP3P water and orange for TIP4PD water) for the PDB and AF model at incubation time point 0.5 min. This time point corresponds to experimental incubation times, not MD simulation time. Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping. Below each absolute value plot, we report the discrepancy, which is defined as the difference between the simulated and experimental deuterated fractions, with the shaded area indicating the corresponding error.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

Reviewer 3 (Public review):

A potential weakness of the study is the usage of equilibrium (unbiased) molecular dynamics simulations, so that processes and conformational changes on the microsecond time scale can be probed. Furthermore, there can be inaccuracies and biases in the description of unfolded peptides and protein segments due to the protein force fields. Here, it should be noted that the authors do acknowledge these possible limitations of their study in the conclusions.

We appreciate the Reviewer’s thoughtful comment. As noted in our response to Reviewer 1, we addressed the concern about sampling by applying orthogonal methods and experimental techniques. We agree with the Reviewer that some form of enhanced sampling is necessary if we want to assess binding in a more quantitative way, e.g., via free energy calculations. However, we also realize that applying any enhanced sampling scheme to our system is very challenging, given its large size and the complex peptide-protein interactions, which are not easily captured in a few collective variables. After a careful assessment and some preliminary tests, we decided that estimating free energies using enhanced sampling would necessitate a separate paper due to both the conceptual complexity of the project and the size of the necessary sampling campaign.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Some enhanced sampling or path sampling simulations may be carried out to identify the peptides’ binding and unbinding mechanisms to the protein. This can show whether the disordered peptides studied in this work do indeed bind to the protein.

We thank the Reviewer for this constructive criticism. We acknowledge the limitations associated with investigating binding and unbinding mechanisms of disordered peptides within the time scales accessible to our equilibrium simulations. However, the primary objective of our study was to sample and characterize a plausible binding pose at the center of the cLD dimer. We wanted to understand if unfolded model peptides require an open groove able to contain them to bind to IRE1’s core luminal domain or if binding also in the absence of an open groove.

Enhanced sampling is, of course, an important strategy to overcome the limits of equilibrium simulations. However, we note that implementing enhanced sampling approaches in this system poses significant challenges due to its large size and the complexity of peptide–protein interactions, which cannot be easily captured using a limited set of collective variables. We decided that a thorough application of enhanced sampling would therefore constitute a separate study. Instead, we decided to validate our simulations in two ways: 1) we ran a new set of free energy calculations, and 2) we tested key predictions in experiments, adding significant new data to strengthen the conclusions of our manuscript.

To evaluate whether the binding free energies of MPZ-derived peptides to human IRE1α cLD dimers are consistent with experimentally reported binding constants, we employed the MM/PBSA (Molecular Mechanics/Poisson–Boltzmann Surface Area) method. Calculations were performed over the final 250 ns of each simulation replica using the Single Trajectory Protocol (STP), which avoids the need for additional simulations. This approach provides an estimate of the effective binding free energy (i.e., enthalpy of binding) by accounting for bonded and non-bonded interactions, as well as solvation contributions. The entropic contribution, being computationally more demanding and subject to additional approximations, was not included. Binding enthalpies were obtained for MPZ1-N (in different initial orientations), MPZ1-C, MPZ1-N-2X, and MPZ1-N-2X-RD. The results indicated small differences in effective binding energies between the shorter peptides (MPZ1-N and MPZ1-C), whereas MPZ1-N-2X exhibited the lowest binding energy and MPZ1-N-2X-RD the highest, consistent with experimental trends. These findings support the reliability of our model and sampling strategy as a framework for analyzing peptide binding conformations to cLD.

We identified residues E102 and Y161 as key contributors to the binding of unfolded peptides in our simulations. Contact analysis revealed these residues as binding hotspots, centrally located within the observed interaction regions. To probe their relevance, we conducted simulations of cLD dimers with single arginine mutations in these residues, aimed at disrupting these hotspots through charge repulsion. These simulations revealed increased instability of the MPZ1N2X on the cLD dimer surface. We further validated these findings experimentally using fluorescence anisotropy assays. Fluorescently labeled MPZ1N-2X was titrated with purified cLD mutants (E102R and Y161R), and anisotropy measurements were fitted to derive  K_1/2 values. Both mutations resulted in approximately a two-fold reduction in binding affinity relative to the wild-type cLD, confirming the importance of these residues in stabilizing peptide binding.

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “Thus, we investigated how the point mutations of two key residues, E102R and Y161R, would affect peptide binding by simulating the cLD mutant in complex with MPZ1N-2X (Fig. 4C-E). We initialized the systems in the pose described for the other peptide-cLD systems described earlier (Fig. 3B, t = 0 µs). In simulations of the wild-type (WT) cLD dimer, the peptide generally remained near the center (Fig. 4C,F). By contrast, MPZ1N-2X displayed reduced binding to E102R, fully dissociating in one TIP4P-D replica (Fig. 4E,F). A similar trend was observed for Y161R, where one partial dissociation event occurred (Fig. 4D,F). Comparative analysis of MPZ1N-2X contact sites on the WT and mutant cLD dimers (Supplementary Fig. 17B-D) revealed that, in the presence of mutations, the peptide engages a broader surface region rather than remaining centrally localized, while forming fewer contacts with the specific residues (Supplementary Fig. 18A-B).”

Addition to the text. (Results section title: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “To experimentally test whether these residues are involved in hIRE1α LD’s interaction with peptides, we expressed and purified these mutants and conducted fluorescence anisotropy experiments using fluorescently labeled MPZ1N-2X peptide. We could purify both E102R and Y161R mutants to high purity (Supplementary Fig. 18C). They both behaved similarly to the wild type during purification. Notably, both E102R and Y161R mutants demonstrated around two-fold lower binding affinity (Fig. 4G, E102  K_1/2= 6.35 µM and Y161R  K_1/2= 5.4 µM, Supplementary Table 1) compared to the wildtype (K_1/2= 2.14 µM, Supplementary Table 1), revealing that the protein’s central area is crucial for binding unfolded proteins and that binding activity occurs within the pocket defined by E102 and Y161.”

Addition to the text. (Figure 4 legend) “(E) Side view snapshot after 1 µs of simulation of E102R hIRE1α cLD dimer (gray) in complex with MPZ1N-2X (orange). The amino acid R102 on both monomers is represented in magenta sticks. (F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Methods section: Binding free energy calculations (MM/PBSA)) “The binding free energy of noncovalently bound complexes of human IRE1 cLD and peptides was calculated with MM/PBSA (Molecular mechanics/PoissonBoltzmann Surface Area) method via gmx_MMPBSA (version 1.6.4)[1, 2]. The Poisson-Boltzmann method was used to estimate the electrostatic contribution to solvation free energy as recommended for data obtained with the CHARMM force field. The contribution of the entropic term was omitted, obtaining effective binding free energy values, or enthalpy of binding (∆H). We used the Single Trajectory Protocol (STP), using the cLD-peptide simulations as input. The calculations were performed on the last 250 ns of each replica. Single-term total non-polar solvation free energy (inp = 1) was used. The charmm_radii (PBRadii= 7) was used to build amber topology files [3]. The default parameters were applied for other terms.”

Addition to the text. (Methods section: Protein purification) “To express hIRE1α LD (24-443) human cDNA sequences were cloned into pET47b(+) to create a coding sequence with N-terminal His6-tag. Mutations of hIRE1α LD were introduced by overlap extension PCR and restriction cloning into pET47b(+). For expression of the proteins, the plasmid of interest was transformed into Escherichia coli strain BL21DE3* RIPL (Agilent Technologies). Cells were grown in Luria Broth until OD600=0.6-0.8. Protein expression was induced with 0.6 mM IPTG, and cells were grown in 20°C overnight. For purification, cells after harvesting were resuspended in Lysis Buffer (50 mM HEPES pH 7.2, 400 mM NaCl, 20 mM imidazole, 5% glycerol, 5 mM β-mercaptoethanol) and were lysed in Constans Systems cell disruptor at 25 000 psi. The supernatant was collected after centrifugation for 45 minutes at 48000×g in 4°C. Supernatant was loaded onto Ni-NTA column (Cytiva) and the protein eluted with a linear gradient of imidazole from 20 to 500 mM. Fractions containing the protein were diluted 1:8 with anion exchange wash buffer (50 mM HEPES pH 7.2, 5 mM β-mercaptoethanol), loaded onto HiTRAP-Q ion exchange column (Cytiva) and eluted with a linear gradient from 50 mM to 1 M NaCl. Afterwards, the His6tag was removed by cleavage with Precission protease (GE Healthcare, 1 µg of enzyme per 100 µg of protein). The cleavage was performed overnight in 4°C. The protein sample after cleavage was loaded onto a Ni-NTA column, and the flow-through containing protein without the tag was collected. The protein was further purified on a Superdex 200 10/300 gel filtration column equilibrated with Buffer A (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT). Protein concentrations were determined using extinction coefficient at 280 nm predicted by the Expasy ProtParam tool (http://web.expasy.org/protparam/).”

Addition to the text. (Methods section: Fluorescence anisotropy) “For fluorescence anisotropy measurements, the MPZ1-N-2X peptide attached to 5 carboxyfluorescein (5-FAM) at its N-terminus was obtained from GenScript at >95% purity. Binding affinities of hIRE1α LD mutants to FAM-labeled peptides were determined by measuring the change in fluorescence anisotropy on a Tecan CM Spark Micro Plate Reader with excitation at 485 nm and emission at 525 nm with increasing concentrations of hIRE1α LD variants. Measurements were performed in Buffer A supplemented with Tween 20 (25 mM HEPES pH 7.2, 150 mM NaCl, 2 mM DTT, 0.025% Tween 20). Fluorescently labeled peptides were used in a concentration of 90 nM. The reaction volume of each data point was 25 µL and the measurements were performed in 384-well, black flat-bottomed plates (Corning) after incubation of peptide with hIRE1α LD variants for 30 min at 25◦C. Binding curves were fitted using Prism Software (GraphPad) using the following equation: F_bound = r_free +( r_max − r_free)/(1+10((Log K_1/2 −x)·n_H)), where F_bound is the fraction of peptide bound, r_max and r_free are the anisotropy values at maximum and minimum plateaus, respectively. n_H is the Hill coefficient and x is the concentration of the protein in log scale. Curve-fitting was performed with minimal constraints to obtain K_1/2 values with high R² values. However, as this equation does not consider the equilibria between hIRE1α LD dimers/oligomers, these apparent K_1/2 values do not reflect the dissociation constant.”

(2) Wherever possible, conclusions related to binding affinity should not be drawn from single unbinding events. For example, the title of Figure 4, "Single point mutation of cLD alters the binding affinity of unfolded peptide," should be softened. Similar changes should be made throughout the manuscript where such claims have been presented.

We thank the Reviewer for highlighting this important point. In the revised manuscript, we have adjusted the text to remove or soften conclusions related to binding affinity that were based on single unbinding events in the MD simulations.

Addition to the text. (Figure 4 title) “Single point mutations of cLD alter the binding of unfolded peptide MPZ1N-2X.”

Addition to the text. (Results section title: Unfolded polypeptides can stably bind to hIRE1α cLD dimer) “Unfolded polypeptides bind to hIRE1α cLD dimer surface.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1αα cLD dimer surface) “Our goal was to elucidate a potential binding pose and identify the relevant features of unfolded proteins and the cLD that affect the binding.”

Reviewer #2 (Recommendations for the authors):

(1) A table of all simulated trajectories, including simulation conditions, number of replicas, box size, number of atoms, equilibration length, recording time step, number of frames for further analysis.

We thank the Reviewer for this helpful suggestion. We have added a summary table of all simulations, including the requested details, to the Supplementary Information (Table 1).

Addition to the text. (Supplementary figures and tables: Table 2)

(2) The current NVT equilibration time was 0.125ns, and then no productive NPT simulations were mentioned as equilibration. Even though this is a simulation of mostly folded structures, it still takes some time for these amino acids to relax within the force field.

We thank the Reviewer for this constructive comment and acknowledge the validity of the concern. However, our simulations were extensively sampled, and equilibration was achieved within the first 50 ns of the production runs. Therefore, the segments of the trajectories from which we draw conclusions correspond to equilibrated states (see RMSD analysis, Figure 1). Additionally, binding free energy calculations (MM/PBSA) were carried out on the last 250 ns of the simulation replicas.

(3) At least three histograms were presented in Figure 2C, which I guess is from multiple simulations, and does not seem to be discussed.

We thank the Reviewer for pointing out the lack of reference to Figure 2C. We added the correct reference to the text where the groove width of luminal domains of human and yeast is discussed.

Author response image 1.

RMSD analysis of human IRE1_α_ cLD dimer simulated in complex with unfolded peptides.

Addition to the text. (Results section: The putative groove of human IREα cLD is dynamic but unable to contain peptides ) In simulations of the dimeric structures, the average groove width was 7.3 ± 0.1 Å for the human cLD and 8.9 ± 0.1 Å for the yeast cLD, averaged over three TIP3P and three TIP4P-D replicas per system (Fig. 2C).

(4) The comment regarding the CHARMM force field on Page 6 is not justified. Actually the force field the authors used (CHARMM36m, Jing et al Nat Methods 2016) did include scaling of TIP3P LJ parameters to correctly capture the dimensions of the intrinsically disordered proteins (IDPs). However, the authors cited a couple of examples of literature of previous versions of CHARMM force fields and commented that it cannot capture IDP dimensions with TIP3P.

We thank the Reviewer for pointing out this source of confusion. We cited the main papers of CHARMM as [4, 5], which were misleading, and following the Reviewer’s advice, we removed these citations.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “Current all-atom force fields used in MD simulations are mainly designed to reproduce the dynamics of folded and globular proteins [6].”

(5) I am fine that the authors used TIP4PD with CHARMM36m, but caution should be taken for such a combination of protein and water force fields. Note that when optimizing force fields for IDPs, one often has to balance protein-water interactions by either enhancing protein-water interactions, enhancing water dispersions, or reducing protein-protein interactions. So, all such optimization is dependent on both protein and water force fields. TIP4PD was designed to pair with Amber99sb-ildn or, most recently, Amber99sb-disp instead of CHARMM36m. This could result in rescaling of LJ parameters.

We thank the Reviewer for raising this issue. We argue that the TIP4P-D water model has been used in combination with the CHARMM36m force field [7] and has been shown to yield satisfactory results for disordered regions.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “The TIP4P-D water model was developed to address limitations of existing force fields in reproducing the structural ensembles of intrinsically disordered proteins and regions. It incorporates enhanced dispersion and moderately stronger electrostatic interactions to improve the balance between water dispersion and electrostatics [8]. Zapletal et al. [7] showed that for proteins containing both folded and disordered regions, the CHARMM36m force field [9] in combination with the TIP4P-D water model provides a robust framework, preventing collapse of disordered regions while preserving folded regions. Acknowledging that the behavior of disordered regions can be case-specific, we conducted molecular dynamics simulations of the two cLD dimer models using the CHARMM36m force field with both TIP3P and TIP4P-D water models.”

(6) I suggest referring to the methodology part for simulation details as much as possible when presenting the story.

We thank the Reviewer for this suggestion. In the revised manuscript, we now refer the reader to the Methodology section for detailed descriptions of the HDX-MS data analysis and the MM/PBSA free energy calculations.

Addition to the text. (Results section: Hydrogen-deuterium exchange experimental data validate the cLD dimer structure) “From our simulations, we calculated the theoretical deuterated fraction using the method by Bradshaw et al.[10] and compared it to the experimental data (Fig. 1C-D and Supplementary Fig. 10) (see Methods).”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “We further assessed the MPZ-derived peptide complexes using MM/PBSA free energy calculations over the final 250 ns of each simulation replica (see Methods), finding binding enthalpies consistent with our observations (Supplementary Fig. 16B). In particular, MPZ1N-2X exhibited the lowest binding energy, whereas MPZ1N-2X-RD showed the highest.”

(7) Error bars and methodology of error analysis should be provided for all cases of all-atom simulations if possible, since convergence is always an issue when considering these conformational changes within microseconds of all-atom simulations.

We thank the Reviewer for the important observation. We agree and added error methodology for the estimation of theoretical deuterated fractions (Fig. 1C).

Addition to the text. (Figure C legend) “Each point represents the mean value derived from three replicas and two monomers per replica. The error bars were obtained from bootstrapping.”

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To reproduce the time points after incubation in deuterium (D₂O), we computed deuterated fractions separately for each of the two monomers constituting a dimer for the time points 0.5 min (30 s) and 5 min (300 s). Then, we computed the mean and standard deviation over the data coming from replicas of the same cLD dimer model (AF or PDB model) and the same water model (TIP3P or TIP4P-D). To estimate the uncertainty of the mean values obtained from our datasets and the dataset from Amin-Wetzel et al. ([11] Figure 3—source data 1), we applied a non-parametric bootstrap resampling procedure. For each sequence range from HDX-MS analysis, we treated the measurements from the N=6 independent datasets as independent samples, accounting for 3 replicas each with two monomers (6 monomers total). We then generated 10,000 bootstrap replicates by sampling the datasets with replacement, maintaining the same number of samples N in each resample. For each replicate, we calculated the mean at each sequence position. The resulting distribution of bootstrap means was used to compute the standard deviation as an estimate of the standard error. We computed the difference between simulation and experimental data (deuterated fraction discrepancy), and for each residue, we selected as the ‘best structure’ the model with the discrepancy closest to zero among PDB-TIP3P, PDB-TIP4P-D, AF-TIP3P, and AF-TIP4P-D systems.”

(8) Technically I would call DR1 and DR2 linker regions within a folded structure. Their motions are quite restrained by the fold part. I therefore, am not sure how much TIP4PD really helps in contrast to a scaled TIP3P. A plot of structures colored with PLDDT score or b-factor within the PDB should be provided. Quantitative metrics of these regions (e.g. chi chi-squared) might help justify the choice of the AF model against the PDB model. Currently, the two models look very similar in Figures 1c and 1d. Similarly, quantitative metrics as a function of different simulation time windows will help justify the convergence of the simulation and indicate the flexibility of these regions.

We thank the Reviewer for this thoughtful comment. In response, we analyzed the AlphaFold2 and AlphaFold3 predictions, which consistently assign very low pLDDT values (<50) to the DR2 region, while DR1, is predicted with higher but still low confidence (50 < pLDDT < 70). These scores indicate intrinsic uncertainty in the structural definition of both regions, supporting their flexibility despite being located within a folded context.

Addition to the text. (Results section: The hIRE1_α_ cLD forms a stable dimer) “All five AlphaFold 2 predictions closely resembled the top-ranked model used for our simulations (Supplementary Fig. 7C). In contrast, the five AlphaFold 3 predictions yielded greater variability in DR2 organization and longer helices in DR2, but still consistently maintain low pLDDT scores in this region, indicating disorder (Supplementary Fig. 7D).”

Addition to the text. (Figure 7 C-D legend) “(C) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT). (D) Superposition of the 5 structures predicted by AlphaFold 3 for the cLD dimer and colored by confidence prediction score (pLDDT).”

(9) Fluorescence anisotropy seems to be an important set of experimental data to justify the binding of multiple unfolded peptides to IRE. I suggest the authors include a bar plot of binding affinity of different variants in Figure 3. The raw titration curves should also be included in SI.

We thank the Reviewer for this valuable suggestion. The binding affinities reported in previous studies are summarized in Table 2; the reader is referred to those works for the corresponding raw titration curves. The binding affinities for the cLD mutants analyzed in the present study are provided in Table 3, and the associated titration curves are shown in Figure 4G.

Addition to the text. (Figure 4G legend) “Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Supplementary figures and tables: Table 3) See Tab. 1

(10) The authors should discuss the dependence of initial orientations of unfolded peptides on the final results. The authors claimed that after 1 microsecond simulations, the orientation of these peptides to IRE changed. Quantitative metrics showing both the binding (e.g., number of contacts) and binding orientation (contact region or angles) should be provided to tell whether the simulation is converged. The comparison to the experimental data lacks quantitative metrics. The authors mentioned the dissociation of MPZ1N-2X-RD in half of the simulations; they might want to provide such a metric for all peptides. Technically, 1 microsecond brute-force simulation is quite short for observing such a binding event, and enhanced sampling methods (e.g. metadynamics) might be necessary for investigating binding. However, at least the presentation and interpretation of the current results should be improved for comparing simulations and experiments.

We thank the Reviewer for the insight. We expanded the discussion of the peptide orientation and added an analysis of the peptide angle with respect to the cLD central groove and contacts. Additionally, we inserted AlphaFold 3 predictions of all the simulated complexes.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0◦ orientation", as the peptide forms a 0 ◦ angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0◦) orientation (Supplementary Fig. 14). We refer to these poses as the "90◦ orientation" and "270◦ orientation".”

Addition to the text. (Supplementary Figures and Tables Fig. 14) “(A) Peptide orientation with respect to the central groove principal axis. The angle was computed as the dihedral angle described by the Cα atoms of Y161 residues (groove principal axis) and the C_α_ atoms of residues L1 and A12 of the MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 10 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between hIRE1α cLD dimer and MPZ1N peptide. The dark lines indicate the rolling average of the fraction of native contacts over 50 frames, while the shaded lines indicate the value per frame. The analysis were performed on three sets of simulations: "90 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis; "270 degrees" orientation, the peptide is initially placed perpendicular to the central groove principal axis but flipped 180 degrees with respect to the 0 degree; "0 degrees" orientation, the peptide is placed parallel to the groove principal axis.”

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1α cLD dimer surface) “AlphaFold3 predictions of the complexes indicate that the peptides adopt the same preferred orientation, despite being predominantly helical (Supplementary Fig. ??A).”

Addition to the text. (Supplementary Figures and Tables Fig. 16A) “(A) Prediction of AlphaFold 3 for hIRE1α cLD dimer in complex with peptides. Colors represent the confidence of the prediction (plDDT).”

(11) I also have a couple of questions regarding the point mutant Y161R. a) The motivation of mutating Y161 to R is more speculative (Figures 4a,b) than quantitative. The authors might want to show an intermolecular contact map between IRE and unfolded peptides or IRE contact probability along residue indexes to show the interaction hotspots. Figure S11 only showed the structure instead of any metrics for such a purpose. b) It might be better to also show a histogram of the distances of Figure 4e and 4f. Figure 4f actually suggested 1 microsecond simulation is quite short to observe the dissociation event. c) Testing the mutation within the experiment, if possible, would clearly strengthen this part of the manuscript.

We thank the Reviewer for these constructive suggestions. We have added an analysis of intermolecular contacts for the Y161R and E102R mutants (Fig. 18A–B), which highlights the interaction hotspots between IRE1 residues and the unfolded peptides. To further characterize peptide–groove interactions, we now provide minimum peptide–groove distance time series for all peptides (Fig. 15B). Moreover, to experimentally support our simulations, we performed fluorescence anisotropy measurements on the MPZ1N-2X peptide with cLD WT and mutant constructs. These experiments confirm our computational observations (Fig. 4F–G and Fig. 18C).

Addition to the text. (Figure 18 legend) “(A) Number of contacts between residues 102 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (B) Number of contacts between residues 161 on both monomers and the MPZ1-N-2X peptide during simulations of WT hIREα LD and mutants E10R and Y161R. The dark lines indicate the rolling average of the fraction of native contacts over 25 frames, while the shaded lines indicate the value per frame. (C) Protein purification of WT hIREα LD and mutants E10R and Y161R.”

Addition to the text. (Figure 4F-G legend) “(F) Time series of the minimum groove-peptide distance for MPZ1N-2X simulated in complex with wild-type, E102R, and Y161R hIRE1α cLD dimer in TIP3P (3 replicas) and TIP4P-D (3 replicas) water. The darker lines show the rolling average over 25 frames, while the shaded lines represent the raw data. (G) Fluorescence anisotropy measurements of labeled MPZ1N-2X binding to hIRE1α LD wild type and mutants E102R and Y161R.”

Addition to the text. (Figure 15B legend) “(B) Minimum groove-peptide distance over time for all simulations of cLD dimer in complex with a peptide. The left column shows the values for the three replicas in TIP3P water, while the right column displays those for the three replicas in TIP4P-D water.”

(12) Similar comments of quantitative analysis (e.g. contact map as a function of simulation time) apply to the last part of results when discussing the intermolecular interactions. Observations such as "the interface predicted by AlphaFold showed stability across MD simulation replicas lasting 200 ns" were provided, but there is no quantitative analysis. How consistent was this observation across multiple replicas of simulations, and how many replicas were used?

We thank the Reviewer for this valuable suggestion. To provide a quantitative assessment, we performed new triplicate simulations of the BiP–cLD monomer complex and plotted the fraction of native contacts over time. These results, which demonstrate the consistency of the interface across replicas, are now included in the Supplementary Material.

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Figure 20 legend) “Fraction of native contacts between BiP and cLD monomer in simulations of the structures predicted by AlphaFold 3 without ligands or in complex with ADP or ATP. The dark lines indicate the rolling average of the fraction of native contacts over 100 frames, while the shaded lines indicate the value per frame. The fraction of native contacts (Q) was calculated according to the definition of Best et al. [12]: . For N pairs of native contacts (i, j), where is the distance of the pair in the initial configuration (here the AlphaFold 3 prediction), r_(i,j)(X) is the distance at frame X, β is a smoothing parameter (β = 50 nm⁻¹), λ is the tolerance of the reference distance (λ \= 1.8) and the cutoff used to define a contact between heavy atoms was 0.45 nm.”

(13) The figure legends are noted using lowercase letters but are described using uppercase.

We thank the Reviewer for pointing that out, and we changed everything to capital letters.

Reviewer #3 (Recommendations for the authors):

(1) Figure 1: I am confused about the HDX-MS results shown in Figure 1. Here, I must also mention that I am not familiar with comparing HDX-MS experiments with MD simulations. The authors mention that they show the deuterated fraction computed from MD simulations for the PDB and AF model at time points 0.5 min and 5 min. However, this time certainly does not correspond to the MD simulation time, thus, it is unclear to me where the difference between the results comes from. Are the two time points some input parameters to the script used to calculate the deuterated fraction? Thus, I would ask the authors to better explain what is the difference in the results between the two time points. Especially, since the general reader might not be familiar with comparing HDX-MS experimental results to MD simulations. Furthermore, I would ask the authors to clarify in the Figure 1 caption that these time points do not correspond to the MD simulation time.

We thank the Reviewer for pointing us to this possible source of confusion. The time points are effectively input parameters to the calculations of theoretical deuterated fractions from MD simulations. We expanded the explanation of the method in the method section and clarified in the Figure 1 caption that these time points do not correspond to the MD simulation time.

Addition to the text. (Methods section: Hydrogen-deuterium exchange fractions calculation from MD simulations) “To determine the deuterated fraction of a peptide segment from simulations, the protection factor for each residue i, Pi, must be computed from the simulation snapshots, following the approach of Best and Vendruscolo [13]: . Here, N_C,i and N_H,i are the number of H-bonds and heavy-atom contacts of the backbone amide of residue i, and the scaling factors β_C and β_H are set to 0.35 and 2.0, respectively. The simulated deuterated fraction of a peptide segment, , defined by residues m_j +1 to n_j, was then calculated at any exchange time point t as:

Where m_j and n_j are the first and last residue numbers of the j-th protein fragment, respectively. The intrinsic exchange rate constants for each residue type () were obtained from Bai et al. with updated acidic residues and glycine [14, 15].”

Addition to the text. (Figure 1 legend: ) “This time point corresponds to experimental incubation times, not MD simulation time.”

Addition to the text. (Figure 10 legend: ) “Time points correspond to experimental incubation times, not MD simulation time.”

(2) For AlphaFold 2 Multimer prediction, the authors only considered the top predicted structure. However, AF2-M, one generally obtains 5 structures, and it is also possible to obtain more structures by using an additional random seed. Thus, it would be interesting if the authors would consider the difference between the 5 structures they obtained from the AF2-M prediction. Are they all very similar? (Especially considering the DR1 and DR2 segments, that is the main difference between the PDB and AF2 structures). Analyzing the different predicted AF2 structures would give more insight into the accuracy of the AF2-M predicted model.

We thank the Reviewer for this insightful suggestion. All AF2-M predicted structures were found to be highly similar, and we now include them in Figure 7E for comparison.

Addition to the text. (Figure 7E legend) “(E) Superposition of the 5 structures predicted by AlphaFold 2 Multimer for the cLD dimer and colored by confidence prediction score (pLDDT).”

(3) On Page 6, the authors talk about a "an early PDB model". First, I find the nomenclature "early" confusing here; perhaps it would be better to talk about "an initial PDB model", but I leave it up to the authors to think about if they want to change that. More importantly, reading the Comp. detail on Page 23, it is not so clear what the difference is between the "early" and "final" PDB models, and how the difference in their setups leads to different results. The information is somewhat there on Page 6 and Page 23, but it can be made much clearer. Thus, I would ask the authors to better explain the difference between the early and final PDB models.

We thank the Reviewer for this helpful comment. In the revised manuscript, we have clarified the terminology and provided a more explicit explanation of the differences between the two IRE1 models, both in the Results section and in the Methods.

Addition to the text. (Results section: The hIRE1α cLD forms a stable dimer) “An initial PDB model with modified side chain orientations in residues L116 and Y166 due to the modelling of neighbouring missing DR1, caused the dimer to dissociate in one-third of the replicas. [...] The final PDB model, with correctly oriented L116 and Y166 (Supplementary Fig. 9B), was stable in simulations in both TIP3P and TIP4P-D water (Supplementary Fig. 7B).”

Addition to the text. (Methods section: IRE1_α_ core Luminal Domain (cLD) structural models - Human PDB dimer) “An initial PDB model was briefly equilibrated in NPT, and a conformation with a groove width of approximately 0.6 nm was selected. This snapshot was used as the initial structure for the initial “PDB model” simulations, in which the dimer dissociates.”

(4) Page 12: "In early simulations", again, I find the nomenclature "early" confusing here. Perhaps it would be better to talk about "In initial simulations" or "In preliminary simulations", but I leave it up to authors to think about this.

We thank the Reviewer for pointing out this possible source of confusion. We improved the text by referring to these simulations based on the different orientations of the peptide on the cLD dimer in the modeled complex.

Addition to the text. (Results section: Unfolded polypeptides bind to hIRE1_α_ cLD dimer surface) “In initial simulations with peptides valine8 and MPZ1-N, we positioned the polypeptides over the cLD, aligning them parallel to the principal axis of the central groove in accordance with the proposed binding mode. We refer to this pose as the "0° orientation", as the peptide forms a 0° angle with the principal axis of the groove. We observed that the peptides could rearrange into an orientation perpendicular to the central groove axis, while maintaining contact with the dimer (Fig. 3A, Supplementary Fig. 13A, valine8 TIP4P-D, and Supplementary Fig. 14). Conversely, when MPZ1-N was initially oriented perpendicularly to the groove, it did not transition to a parallel (0°) orientation (Supplementary Fig. 14). We refer to these poses as the "90° orientation" and "270° orientation".”

Here, we provide a detailed description of the additional changes made to the manuscript.

Additional edits to the manuscript

Following discussions with Prof. Dr. David Ron, we refined our BiP model by removing the signal peptide (residues 1–18). Using AlphaFold 3, we predicted BiP–cLD heterodimeric complexes in the presence of ADP, ATP, or without nucleotide. Each of the three complexes was simulated in TIP3P water, in three independent replicas of 1 µs each.

Addition to the text. (Results section: hIRE1α cLD intermolecular interactions guide the activation process) “We used AlphaFold 3 to model the interaction between a cLD monomer and BiP (residues E19–L654) in the presence of ATP and ADP (Fig. 5B, Supplementary Fig. 19A). Prediction quality was limited in the apo and ADP-bound states (pTM = 0.48, ipTM = 0.59; pTM = 0.49, ipTM = 0.61, respectively), whereas ATP binding improved accuracy (pTM = 0.66, ipTM = 0.72). The predicted interfaces involved DR2, particularly residues 314PLLEG-318, forming a short parallel β-sheet with the substrate-binding domain (SBD) of BiP through two hydrogen bonds. All AlphaFold 3 models were stable across three 1-µs simulations (Supplementary Fig. 19B), with cLD–BiP interfaces retaining 60–80% of initial contacts (Supplementary Fig. 20). In the apo and ADP-bound states, the nucleotide-binding domain (NBD) showed high Predicted Aligned Error (PAE) relative to the cLD, indicating uncertain positioning of the two domains relative to each other. Notably, in the ADP-bound state, which is thought to interact with hIRE1α cLD, the NBD remained mobile but proximal to the αB-helices, thereby restricting access to this region. Together, the AlphaFold 3 predictions suggest that BiP engages hIRE1α cLD by sterically hindering the oligomerization interface defined by DR2 and the αB-helices [16].”

Addition to the text. (Figure 5 legend) “(B) BiP-cLD monomer complex as predicted by AlphaFold (BiP in shades of purple, cLD in orange) before the simulation (t = 0 µs) and at the end of the simulation (t = 1 µs). The SBD (residues E19-D408) is colored in light purple, and the NDB (residues C420-E650) in dark purple, and the interdomain linker (residues D409-V419) and KDEL motif (residues K651-L654) in light purple.”

Addition to the text. (Figure 19 legend) “(A) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ATP-bound BiP. The colors are as in Fig. 5B. (B) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with ADP-bound BiP. (C) Prediction of AlphaFold 3 for hIRE1α cLD monomer in complex with BiP not bound to any nucleotide. (D) Structure of hIRE1α cLDBiP-ATP after 2 µs of simulation. (E) Structure of hIRE1α cLD-BiP-ADP after 2 µs of simulation. (F) Structure of hIRE1α cLD-BiP after 2 µs of simulation.”

Addition to the text. (Methods section: cLD monomer in complex with BiP) “The BiP-cLD heterodimer systems were predicted with AlphaFold 3 using the AlphaFold server[17] at https://alphafoldserver.com/. The hIRE1α cLD sequence used is the same used for predicting the dimer: the PDB 2HZ6 sequence, Uniprot identifier O75460 with mutations C127S and C311S, and residues P29-P368. The BiP sequence used is taken from UniProt identifier P11021, residues E19L654. We predicted three complexes: one without any nucleotide, one containing ADP, and another containing ATP. Simulations of the BiP-cLD complex were run in TIP3P water.”

We have updated the Zenodo repository with additional data and calculations, and the corresponding link is provided in the manuscript.

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eLife Assessment

This manuscript reports high-resolution cryo-EM structures of a trimethylamine N-oxide demethylase and advances the hypothesis that the enzyme is bifunctional, coupling TMAO demethylation to formaldehyde capture via an enclosed intramolecular tunnel. The structural findings remain valuable, particularly the unusual oligomeric architecture and proposed conduit for a reactive intermediate. While the revision improves clarity and addresses several technical concerns, the central mechanistic framework remains incomplete, with persistent concerns regarding the proposed catalytic mechanism and metal dependence.

Reviewer #1 (Public review):

Summary:

Thach et al. report on the structure and function of trimethylamine N-oxide demethylase (TDM). They identify a novel complex assembly composed of multiple TDM monomers and obtain high-resolution structural information for the catalytic site, including an analysis of its metal composition, which leads them to propose a mechanism for the catalytic reaction.

In addition, the authors describe a novel substrate channel within the TDM complex that connects the N-terminal ZnZn²⁺-dependent TMAO demethylation domain with the C-terminal tetrahydrofolate (THF)-binding domain. This continuous intramolecular tunnel appears highly optimized for shuttling formaldehyde (HCHO), based on its negative electrostatic properties and restricted width. The authors propose that this channel facilitates the safe transfer of HCHO, enabling its efficient conversion to methylenetetrahydrofolate (MTHF) at the C-terminal domain as a microbial detoxification strategy. Experimental data that shows an involvement of TDM in the reaction of HCHO with THF is less convincing.

Strengths:

The authors provide convincing high-resolution cryo-EM structural evidence (up to 2 Å) revealing an intriguing complex composed of two full monomers and two half-domains. They further present evidence for the metal ion bound at the active site and articulate a hypothesis for the catalytic cycle. Substantial effort is devoted to optimizing and characterizing enzyme activity, including detailed kinetic analyses across a range of pH values, temperatures, and substrate concentrations. Furthermore, the authors validate their structural insights through functional analysis of active-site point mutants.

In addition, the authors identify a continuous channel for formaldehyde (HCHO) passage within the structure and support this interpretation through molecular dynamics simulations. These analyses suggest an exciting mechanism of specific, dynamic, and gated channelling of HCHO. This finding is particularly appealing, as it implies the existence of a unique, completely enclosed conduit that may be of broad interest, including potential applications in bioengineering.

Weaknesses:

Although the idea of an enclosed channel for HCHO is compelling, the experimental evidence supporting enzymatic assistance in the reaction of HCHO with THF is less convincing. The linear regression analysis shown in Figure 1C demonstrates a THF concentration-dependent decrease in HCHO; however, it is well established that HCHO and THF can react spontaneously in a non-enzymatic manner, raising the possibility that the observed effect does not require enzymatic involvement. I appreciate the authors' clarification that the data in Figure 1 were not intended to demonstrate enzymatic channelling or catalytic involvement in the HCHO-THF reaction, and that the assay does not distinguish between changes in HCHO production and downstream consumption. However, the statement "these findings show that TDM carries out two linked reactions: TMAO demethylation at one active site, and the HCHO produced can condense with THF at the C-terminal domain, connecting TMAO breakdown to one-carbon metabolism" (page 2) still implies a mechanistic and functional coupling that is not supported by the presented data and appears inconsistent with the authors' clarification. In light of this, I recommend revising this statement to avoid implying mechanistic or functional coupling between the two reactions unless additional experimental evidence is provided.

Overall, the authors were successful in advancing our structural and functional understanding of the TDM complex. They suggest an interesting oligomeric complex composition which should be investigated with additional biophysical techniques.

Additionally, they provide an intriguing hypothesis for a new type of substrate channelling. Additional kinetic experiments focusing on HCHO and THF turnover by enzymatic proximity effects would strengthen this potentially fundamental finding. If this channelling mechanism can be supported by stronger experimental evidence, it would substantially advance our understanding and knowledge of biologic conduits and enable future efforts in the design of artificial cascade catalysis systems with high conversion rate and efficiency, as well as detoxification pathways.

Reviewer #2 (Public review):

Summary:

The manuscript reports a cryo-EM structure of TMAO demethylase from Paracoccus sp. This is an important enzyme in the metabolism of trimethylamine oxide (TMAO) and trimethylamine (TMA) in human gut microbiota, so new information about this enzyme would certainly be of interest.

Strengths:

The cryo-EM structure for this enzyme is new and provides new insights into the function of the different protein domains, and a channel for formaldehyde between the two domains.

Weaknesses:

(1) The proposed catalytic mechanism in this manuscript does not make sense. Previous mechanistic studies on the Methylocella silvestris TMAO demethylase (FEBS Journal 2016, 283, 3979-3993, reference 7) reported that, as well as a Zn2+ cofactor, there was a dependence upon non-heme Fe2+, and proposed a catalytic mechanism involving deoxygenation to form TMA and an iron(IV)-oxo species, followed by oxidative demethylation to form DMA and formaldehyde.

In this work, the authors do not mention the previously proposed mechanism, but instead just say that elemental analysis "excluded iron". This is alarming, since the previous work has a key role for non-heme iron in the mechanism. The elemental analysis here gives a Zn content of about 0.5 mol/mol protein (and no Fe), whereas the Methylocella TMAO demethylase was reported to contain 0.97 mol Zn/mol protein, and 0.35-0.38 mol Fe/mol protein. It does, therefore, appear that their enzyme is depleted in Zn, and the absence of Fe impacts on the mechanism, as explained below.

The proposed catalytic mechanism in this manuscript, I am sorry to say, does not make sense, for several reasons:

i) Demethylation to form formaldehyde is not a hydrolytic process; it is an oxidative process (normally accomplished by either cytochrome P450 or non-heme iron-dependent oxygenase). The authors propose that a zinc (II) hydroxide attacks the methyl group, which (a) is unprecedented, (b) even if it were possible, would generate methanol, not formaldehyde.

ii) The amine oxide is proposed to deoxygenate, with hydroxide appearing on the Zn - unfortunately, amine oxide deoxygenation is a reductive process, for which a reducing agent is needed, and Zn2+ is not a redox active metal ion;

iii) The authors say "forming a tetrahedral intermediate, as described for metalloprotease" but zinc metalloproteases attack an amide carbonyl to form an oxyanion intermediate, whereas in this mechanism there is no carbonyl to attack, so this statement is just wrong.

So on several counts the proposed mechanism cannot be correct. Some redox cofactor is needed in order to carry out amine oxide deoxygenation, and Zn2+ cannot fulfil that role. Fe2+ could do, which is why the previously proposed mechanism involving an iron(IV)-oxo intermediate is feasible. But the authors claim that their enzyme has no Fe. If so then there must be some other redox cofactor present. Therefore, the authors need to re-analyse their enzyme carefully and look either for Fe or for some other redox-active metal ion, and then provide convincing experimental evidence for a feasible catalytic mechanism. As it stands the proposed catalytic mechanism is unacceptable.

Revised version. The authors have essentially not changed the proposed mechanism. They have removed the reference to zinc metalloproteases, but still propose a mechanism mediated only by Zn2+. As explained above, attack by zinc (II) hydroxide is unprecedented and would generate methanol, not formaldehyde, and amine deoxygenation is a reductive process that cannot be fulfilled by Zn2+. So the proposed mechanism is still not feasible at all. The authors now say that "oxidative chemistry....remains unresolved", I'm sorry, but that is not acceptable.

I have urged the authors to re-examine the metal content of their enzyme, In the Supporting Information (Figure S5) they give ICPMS data that indicates a Zn stoichiometry of 0.5 mol Zn/mol protein, and Fe is not detected. Have the authors analysed for other redox active metals? The authors say that there is no evidence for any other metal binding site, but there is only 50% occupancy of Zn in their protein, so could there be a different metal ion present in place of Zn in the other 50% of the protein, that accounts for the observed activity?

Since there is clearly a major discrepancy here, the onus is on the authors to explain the discrepancy, rather than just returning with the same data. For example, they could treat the enzyme with EDTA to remove all metals (and check the treated enzyme by ICPMS), and then add different metal ions to test activity with different metals (could even titrate with different molar equivalents of metal ions). They could then test a range of different redox-active metal ions.

(2) Given the metal content reported here, it is important to be able to compare the specific activity of the enzyme reported here with earlier preparations. The authors have now done this in the revised version.

(3) The consumption of formaldehyde to form methylene-THF is potentially interesting, but the authors say "HCHO levels decreased in the presence of THF", which could potentially be due to enzyme inhibition by THF. Is there evidence that this is a time-dependent and protein-dependent reaction? Not yet addressed.

Also in Figure 1C, HCHO reduction (%) is not very helpful, because we don't know what concentration of formaldehyde is formed under these conditions; it would be better to quote in units of concentration, rather than %. This point has been addressed by the authors in the revised version.

(4) Has this particular TMAO demethylase been reported before? It's not clear which Paracoccus strain the enzyme is from; the Experimental Section just says "Paracoccus sp.", which is not very precise. There has been published work on the Paracoccus PS1 enzyme, is that the strain used? Details about the strain are needed, and the accession for the protein sequence. Addressed in the revised version.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Thach et al. report on the structure and function of trimethylamine N-oxide demethylase (TDM). They identify a novel complex assembly composed of multiple TDM monomers and obtain high-resolution structural information for the catalytic site, including an analysis of its metal composition, which leads them to propose a mechanism for the catalytic reaction.

In addition, the authors describe a novel substrate channel within the TDM complex that connects the N-terminal Zn²-dependent TMAO demethylation domain with the C-terminal tetrahydrofolate (THF)-binding domain. This continuous intramolecular tunnel appears highly optimized for shuttling formaldehyde (HCHO), based on its negative electrostatic properties and restricted width. The authors propose that this channel facilitates the safe transfer of HCHO, enabling its efficient conversion to methylenetetrahydrofolate (MTHF) at the C-terminal domain as a microbial detoxification strategy.

Strengths:

The authors provide convincing high-resolution cryo-EM structural evidence (up to 2 Å) revealing an intriguing complex composed of two full monomers and two half-domains. They further present evidence for the metal ion bound at the active site and articulate a plausible hypothesis for the catalytic cycle. Substantial effort is devoted to optimizing and characterizing enzyme activity, including detailed kinetic analyses across a range of pH values, temperatures, and substrate concentrations. Furthermore, the authors validate their structural insights through functional analysis of active-site point mutants.

In addition, the authors identify a continuous channel for formaldehyde (HCHO) passage within the structure and support this interpretation through molecular dynamics simulations. These analyses suggest an exciting mechanism of specific, dynamic, and gated channeling of HCHO. This finding is particularly appealing, as it implies the existence of a unique, completely enclosed conduit that may be of broad interest, including potential applications in bioengineering.

Weaknesses:

Although the idea of an enclosed channel for HCHO is compelling, the experimental evidence supporting enzymatic assistance in the reaction of HCHO with THF is less convincing. The linear regression analysis shown in Figure 1C demonstrates a THF concentration-dependent decrease in HCHO, but the concentrations used for THF greatly exceed its reported KD (enzyme concentration used in this assay is not reported). It has previously been shown that HCHO and THF can couple spontaneously in a non-enzymatic manner, raising the possibility that the observed effect does not require enzymatic channeling. An additional control that can rule out this possibility would help to strengthen the evidence. For example, mutating the THF binding site to prevent THF binding to the protein complex could clarify whether the observed decrease in HCHO depends on enzyme-mediated proximity effects. A mutation which would specifically disable channeling could be even more convincing (maybe at the narrowest bottleneck).

We agree with the reviewer that HCHO and THF can react spontaneously in a non-enzymatic manner, and our experiments were not intended to demonstrate enzymatic channeling. The linear regression analysis in Figure 1C was designed solely to confirm that HCHO reacts with THF under our assay conditions. Accordingly, THF was titrated over a broad concentration range starting from zero, and the observed THF concentration–dependent decrease in HCHO reflects this chemical reactivity.

We do not interpret these data as evidence that the enzyme catalyzes or is required for the HCHO–THF coupling reaction. Instead, the structural observation of an enclosed channel is presented as a separate finding. We have clarified this point in the revised text to avoid overinterpretation of the biochemical data (page 2, line 16).

Another concern is that the observed decrease in HCHO could alternatively arise from a reduced production of HCHO due to a negative allosteric effect of THF binding on the active site. From this perspective, the interpretation would be more convincing if a clear coupled effect could be demonstrated, specifically, that removal of the product (HCHO) from the reaction equilibrium leads to an increase in the catalytic efficiency of the demethylation reaction.

We agree that, in principle, a decrease in detectable HCHO could also arise from an indirect effect of THF binding on enzyme activity. However, in our study the experiment was not designed to assess catalytic coupling or allosteric regulation. The assay in question monitors HCHO levels under defined conditions and does not distinguish between changes in HCHO production and downstream consumption.

Additionally, we do not interpret the observed decrease in HCHO as evidence that THF binding enhances catalytic efficiency, or that removal of HCHO shifts the reaction equilibrium. Instead, the data are presented to establish that HCHO can react with THF under the assay conditions. Any potential allosteric effects of THF on the demethylation reaction, or kinetic coupling between HCHO removal and catalysis, are beyond the scope of the current study, and are not claimed.

While the enzyme kinetics appear to have been performed thoroughly, the description of the kinetic assays in the Methods section is very brief. Important details such as reaction buffer composition, cofactor identity and concentration (Zn²⁺), enzyme concentration, defined temperature, and precise pH are not clearly stated. Moreover, a detailed methodological description could not be found in the cited reference (6), if I am not mistaken.

Thank you for the suggestion. We have added reference [24] to the methodological description on page 8. The Methods section has been revised accordingly on page 8 under “TDM Activity Assay,” without altering the Zn²⁺ concentration.

The composition of the complex is intriguing but raises some questions. Based on SDS-PAGE analysis, the purified protein appears to be predominantly full-length TDM, and size-exclusion chromatography suggests an apparent molecular weight below 100 kDa. However, the cryo-EM structure reveals a substantially larger complex composed of two full-length monomers and two half-domains.

We appreciate the reviewer’s careful analysis of the apparent discrepancy between the biochemical characterization and the cryo-EM structure. This issue is addressed in Figure S1, which may have been overlooked.

As shown in Figure S1, the stability of TDM is highly dependent on protein and salt conditions. At 150 mM NaCl, SEC reveals a dominant peak eluting between 10.5 and 12 mL, corresponding to an estimated molecular weight of ~170–305 kDa (blue dot, Author response image 1). This fraction was explicitly selected for cryo-EM analysis and yields the larger complex observed in the reconstruction. At lower salt concentrations (50 mM) or higher (>150 mM NaCl), the protein either aggregates or elutes near the void volume (~8 mL).

SDS–PAGE analysis detects full-length TDM together with smaller fragments (~40–50 kDa and ~22–25 kDa). The apparent predominance of full-length protein on SDS–PAGE likely reflects its greater staining intensity per molecule and/or a higher population, rather than the absence of truncated species.

Author response image 1.

Given the lack of clear evidence for proteolytic fragments on the SDS-PAGE gel, it is unclear how the observed stoichiometry arises. This raises the possibility of higher-order assemblies or alternative oligomeric states. Did the authors attempt to pick or analyze larger particles during cryo-EM processing? Additional biophysical characterization of particle size distribution - for example, using interferometric scattering microscopy (iSCAT)-could help clarify the oligomeric state of the complex in solution.

Cryo-EM data were collected exclusively from the size-exclusion chromatography fraction eluting between 10.5 and 12 mL. This fraction was selected to isolate the dominant assembly in solution. Extensive 2D and 3D particle classification did not reveal distinct classes corresponding to smaller species or higher-order oligomeric assemblies. Instead, the vast majority of particles converged to a single, well-defined structure consistent with the 2 full-length + 2 half-domain stoichiometry.

A minor subpopulation (~2%) exhibited increased flexibility in the N-terminal region of the two full-length subunits, but these particles did not form a separate oligomeric class, indicating conformational heterogeneity rather than alternative assembly states (Author response image 2). Together, these data support the 2+2½ architecture as the predominant and stable complex under the conditions used for cryo-EM. Additional techniques, such as iSCAT, would provide complementary information, but are not required to support the conclusions drawn from the SEC and cryo-EM analyses presented here.

Author response image 2.

The authors mention strict symmetry in the complex, yet C2 symmetry was enforced during refinement. While this is reasonable as an initial approach, it would strengthen the structural interpretation to relax the symmetry to C1 using the C2-refined map as a reference. This could reveal subtle asymmetries or domain-specific differences without sacrificing the overall quality of the reconstruction.

We thank the reviewer for this thoughtful suggestion. In standard cryo-EM data processing, symmetry is typically not imposed initially to minimize potential model bias; accordingly, we first performed C1 refinement before applying C2 symmetry. The resulting C1 reconstructions revealed no detectable asymmetry or domain-specific differences relative to the C2 map. In addition, relaxing the symmetry consistently reduced overall resolution, indicating lower alignment accuracy and further supporting the presence of a predominantly symmetric assembly.

In this context, the proposed catalytic role of Zn²⁺ raises additional questions. Why is a 2:1 enzyme-to-metal stoichiometry observed, and how does this reconcile with previous reports? This point warrants discussion. Does this imply asymmetric catalysis within the complex? Would the stoichiometry change under Zn²⁺-saturating conditions, as no Zn²⁺ appears to be added to the buffers? It would be helpful to clarify whether Zn²⁺ occupancy is equivalent in both active sites when symmetry is not imposed, or whether partial occupancy is observed.

The observed ~2:1 enzyme-to-Zn²⁺ stoichiometry likely reflects the composition of the 2 full-length + 2 half-domain (2+2½) complex. In this assembly, only the core domains that are fully present in the complex contribute to metal binding. The truncated or half-domains lack the Zn²⁺ binding domain. As a result, only two metal-binding sites are occupied per assembled complex, consistent with the measured stoichiometry.

We note that Zn²⁺ was not deliberately added to the buffers, so occupancy may not reflect full saturation. Based on our cryo-EM and biochemical data, both metal-binding sites in the full-length subunits appear to be occupied to an equivalent extent, and no clear evidence of asymmetric catalysis is observed under these current experimental conditions. Full Zn²⁺ saturation could potentially increase occupancy, but was not explored in these experiments.

The divalent ion Zn²⁺ is suggested to activate water for the catalytic reaction. I am not sure if there is a need for a water molecule to explain this catalytic mechanism. Can you please elaborate on this more? As one aspect, it might be helpful to explain in more detail how Zn-OH and D220 are recovered in the last step before a new water molecule comes in.

Thank you for your suggestion. We revised our text in page 2 as bellow.

Based on our structural and biochemical data, we propose a structurally informed working model for TMAO turnover by TDM (Scheme 1). In this model, Zn²⁺ plays a non-redox role by polarizing the O–H bond of the bound hydroxyl, thereby lowering its pK_a. The D220 carboxylate functions as a general base, abstracting the proton to generate a hydroxide nucleophile. This hydroxide then attacks the electrophilic N-methyl carbon of TMAO, forming a tetrahedral carbinolamine (hemiaminal) intermediate. Subsequent heterolytic cleavage of the C–N bond leads to the release of HCHO. D220 then switches roles to act as a general acid, donating a proton to the departing nitrogen, which facilitates product release and regenerates the active site. This sequence allows a new water molecule to rebind Zn²⁺, enabling subsequent catalytic turnovers. This proposed pathway is consistent with prior mechanistic studies, in which water addition to the azomethine carbon of a cationic Schiff base generates a carbinolamine intermediate, followed by a rate-limiting breakdown to yield an amino alcohol and a carbonyl compound, in the published case, an aldehyde (Pihlaja et al., J. Chem. Soc. Perkin Trans. 2, 1983, 8, 1223–1226).

Overall, the authors were successful in advancing our structural and functional understanding of the TDM complex. They suggest an interesting oligomeric complex composition which should be investigated with additional biophysical techniques.

Additionally, they provide an intriguing hypothesis for a new type of substrate channeling. Additional kinetic experiments focusing on HCHO and THF turnover by enzymatic proximity effects would strengthen this potentially fundamental finding. If this channeling mechanism can be supported by stronger experimental evidence, it would substantially advance our understanding and knowledge of biologic conduits and enable future efforts in the design of artificial cascade catalysis systems with high conversion rate and efficiency, as well as detoxification pathways.

Reviewer #2 (Public review):

Summary:

The manuscript reports a cryo-EM structure of TMAO demethylase from Paracoccus sp. This is an important enzyme in the metabolism of trimethylamine oxide (TMAO) and trimethylamine (TMA) in human gut microbiota, so new information about this enzyme would certainly be of interest.

Strengths:

The cryo-EM structure for this enzyme is new and provides new insights into the function of the different protein domains, and a channel for formaldehyde between the two domains.

Weaknesses:

(1) The proposed catalytic mechanism in this manuscript does not make sense. Previous mechanistic studies on the Methylocella silvestris TMAO demethylase (FEBS Journal 2016, 283, 3979-3993, reference 7) reported that, as well as a Zn2+ cofactor, there was a dependence upon non-heme Fe2+, and proposed a catalytic mechanism involving deoxygenation to form TMA and an iron(IV)-oxo species, followed by oxidative demethylation to form DMA and formaldehyde.

In this work, the authors do not mention the previously proposed mechanism, but instead say that elemental analysis "excluded iron". This is alarming, since the previous work has a key role for non-heme iron in the mechanism. The elemental analysis here gives a Zn content of about 0.5 mol/mol protein (and no Fe), whereas the Methylocella TMAO demethylase was reported to contain 0.97 mol Zn/mol protein, and 0.35-0.38 mol Fe/mol protein. It does, therefore, appear that their enzyme is depleted in Zn, and the absence of Fe impacts the mechanism, as explained below.

The proposed catalytic mechanism in this manuscript, I am sorry to say, does not make sense to me, for several reasons:

(i) Demethylation to form formaldehyde is not a hydrolytic process; it is an oxidative process (normally accomplished by either cytochrome P450 or non-heme iron-dependent oxygenase). The authors propose that a zinc (II) hydroxide attacks the methyl group, which is unprecedented, and even if it were possible, would generate methanol, not formaldehyde.

(ii) The amine oxide is then proposed to deoxygenate, with hydroxide appearing on the Zn - unfortunately, amine oxide deoxygenation is a reductive process, for which a reducing agent is needed, and Zn2+ is not a redox-active metal ion;

(iii) The authors say "forming a tetrahedral intermediate, as described for metalloproteinase", but zinc metalloproteases attack an amide carbonyl to form an oxyanion intermediate, whereas in this mechanism, there is no carbonyl to attack, so this statement is just wrong.

So on several counts, the proposed mechanism cannot be correct. Some redox cofactor is needed in order to carry out amine oxide deoxygenation, and Zn2+ cannot fulfil that role. Fe2+ could do, which is why the previously proposed mechanism involving an iron(IV)-oxo intermediate is feasible. But the authors claim that their enzyme has no Fe. If so, then there must be some other redox cofactor present. Therefore, the authors need to re-analyse their enzyme carefully and look either for Fe or for some other redox-active metal ion, and then provide convincing experimental evidence for a feasible catalytic mechanism. As it stands, the proposed catalytic mechanism is unacceptable.

We thank the reviewer for the detailed and thoughtful mechanistic critique. We fully agree that Zn²⁺ is not redox-active, and cannot directly mediate oxidative demethylation or amine oxide deoxygenation. We acknowledge that the oxidative step required for the conversion of TMAO to HCHO is not explicitly resolved in the present study. Accordingly, we have revised the manuscript to remove any implication of Zn²⁺-mediated redox chemistry, and have eliminated the previously imprecise analogy to zinc metalloproteases.

We recognize and now discuss prior biochemical work on TMAO demethylase from Methylocella silvestris (MsTDM), which proposed an iron-dependent oxidative mechanism (Zhu et al., FEBS 2016, 3979–3993). That study reported approximately one Zn²⁺ and one non-heme Fe²⁺ per active enzyme, implicated iron in catalysis through homology modeling and mutagenesis, and used crossover experiments suggesting a trimethylamine-like intermediate and oxygen transfer from TMAO, consistent with an Fe-dependent redox process. However, that system lacked experimental structural information, and did not define discrete metal-binding sites.

In contrast,

(1) Our high-resolution cryo-EM structures and metal analyses of TDM consistently reveal only a single, well-defined Zn²⁺-binding site, with no structural evidence for an additional iron-binding site as in the previous report (Zhu et al., FEBS 2016, 3979–3993).

(2) To investigate the potential involvement of iron, we expressed TDM in LB medium supplemented with Fe(NH₄)₂SO₄ and determined its cryo-EM structure. This structure is identical to the original one, and no EM density corresponding to a second iron ion was observed. Moreover, the previously proposed Fe²⁺-binding residues are spatially distant (Figure S6).

(3) ICP-MS analysis shows undetectable Iron, and only Zinc ion (Figure S5).

(4) Our enzyme kinetics analysis with the TDM without Iron is comparable to that of from MsTDM (Figure 1A). The differences in Km and Vmax we propose is due to the difference in the overall sequence of the enzymes. Please also see comment at the end on a new published paper on MsTDM.

While we cannot comment on the MsTDM results, our ‘experimental’ results do not support the presence of an iron-binding site. Our data indicate that this chemistry is unlikely to be mediated by a canonical non-heme iron center as proposed for MsTDM. We therefore revised our model as a structural framework that rationalizes substrate binding, metal coordination, and product stabilization, while clearly delineating the limits of mechanistic inference supported by the current data.

The scheme 1 and proposal mechanism section were revised in page 4. Figure S6 was added.

(2) Given the metal content reported here, it is important to be able to compare the specific activity of the enzyme reported here with earlier preparations. The authors do quote a Vmax of 16.52 µM/min/mg; however, these are incorrect units for Vmax, they should be µmol/min/mg. There is a further inconsistency between the text saying µM/min/mg and the Figure saying µM/min/µg.

Thank you for the correction. We converted the V_max unit to nmol/min/mg. and revised the text in page 2. We also compared with the value of the previous report in the TDM enzyme by revising the text on page 2. See also the note on a newly published manuscript and its comparison.

(3) The consumption of formaldehyde to form methylene-THF is potentially interesting, but the authors say "HCHO levels decreased in the presence of THF", which could potentially be due to enzyme inhibition by THF. Is there evidence that this is a time-dependent and protein-dependent reaction? Also in Figure 1C, HCHO reduction (%) is not very helpful, because we don't know what concentration of formaldehyde is formed under these conditions; it would be better to quote in units of concentration, rather than %.

We appreciate this important point. We have revised Figure 1C to present HCHO levels in absolute concentration units. While the current data demonstrate reduced detectable HCHO in the presence of THF, we agree that distinguishing between HCHO consumption and potential THF-mediated enzyme inhibition would require dedicated time-course and protein-dependence experiments. We have therefore revised the description to avoid overinterpretation and limit our conclusions to the observed changes in HCHO concentration in page 2, line 18-19.

(4) Has this particular TMAO demethylase been reported before? It's not clear which Paracoccus strain the enzyme is from; the Experimental Section just says "Paracoccus sp.", which is not very precise. There has been published work on the Paracoccus PS1 enzyme; is that the strain used? Details about the strain are needed, and the accession for the protein sequence.

Thank you for this comment. We now indicate that the enzyme is derived from Paracoccus sp. DMF and provide the accession number for the protein sequence (WP_263566861) in the Experimental Section (page 8, line 4).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The ITC experiment requires a ligand-into-buffer titration as an additional control. Also, maybe I misunderstood the molar ratio or the concentrations you used, but if you indeed added a total of 4.75 μL of 20 μM THF into 250 μL of 5 μM TDM, it is not clear to me how this leads to a final molar ratio of 3.

We thank the reviewer for this suggestion. A ligand-into-buffer control ITC experiment was performed and is now included in Figure S8C, which shows no realizable signal.

Regarding the molar ratio, it is our mistake. The experiment used 2.45 μL injections of 80 μM THF into 250 μL of 5 μM TDM. This corresponds to a final ligand concentration of ~12.8 μM, giving a ligand-to-protein molar ratio of ~2.6. We revised our text in page 9, ITC section.

(2) Characterization/quality check of all mutant enzymes should be performed by NanoDSF, CD spectroscopy or similar techniques to confirm that proteins are properly folded and fit for kinetic testing.

We appreciate the reviewer’s suggestion. All mutant proteins, including D220A, D367A, and F327A, were purified with yields similar to the wild-type enzyme. Additionally, cryo-EM maps of the mutants show well-defined density and overall structural integrity consistent with the wild-type. These findings indicate that the introduced mutations do not significantly affect protein folding, supporting their use for kinetic analysis. While NanoDSF might reveal differences in thermal stability due to mutations, it does not provide structural information. Our conclusions are not based on minor differences in thermostability. Our cryo-EM structures of the mutants offer much more reliable structural data than CD spectroscopy.

(3) Best practice would suggest overlapping pH ranges between different buffer systems in the pH-dependence experiments to rule out buffer-specific effects independent of pH.

We thank the reviewer for this helpful suggestion. We agree that overlapping pH ranges between different buffer systems can be valuable for excluding buffer-specific effects. In this study, the pH-dependence experiments were intended to provide a qualitative assessment of pH sensitivity rather than a detailed analysis of buffer-independent pKa values. While we cannot fully exclude minor buffer-specific contributions, the overall trends observed were reproducible and sufficient to support the conclusions drawn. We have added a clarifying statement to the revised manuscript to reflect this consideration, page 2, line 12.

(4) Structural comparison revealed high similarity to a THF-binding protein, with superposition onto a T protein.": It would be nice to show this as an additional figure, as resolution and occupancy for THF are low.

We thank the reviewer for this suggestion. To address this point, we have revised Figure S6 by adding an additional panel (C, now is Figure S7C) showing the structural superposition of TDM with the THF-binding T protein. This comparison is included to better illustrate the structural similarity, despite the limited resolution and partial occupancy of THF density in our map.

(5) Editing could have been done more thoroughly. Some spelling mistakes, e.g. "RESEULTS", "redius", "complec"; kinetic rate constants should be written in italic (not uniform between text and figures); Prism version is missing; Vmax of 16.52 µM/min/mg - doublecheck units; Figure S1B: The "arrow on the right" might have gone missing.

We corrected the spelling in page 2 ~ line 10, page 5 ~ line 34, page 6 ~ line40. All were highlighted as blue color. Prism version was added. The arrow was added into figure S1B. The Vmax unit is corrected to nmol/min/mg

Reviewer #2 (Recommendations for the authors):

(1) The authors must re-examine the metal content of their purified enzyme, looking in particular for Fe or another redox-active metal ion, which could be involved in a reasonable catalytic mechanism.

We thank the reviewer for this suggestion and have carefully re-examined the metal content of TDM. Elemental analyses by EDX and ICP-MS consistently detected Zn²⁺ in purified TDM (Zn:protein ≈ 1:2), whereas Fe was below the detection limit across multiple independent preparations (Fig. S5A,B). To assess whether iron could be incorporated or play a functional role, we expressed TDM in E. coli grown in LB medium supplemented with Fe(NH₄SO₄)₂ and performed activity assays in the presence of exogenous Fe²⁺. Neither condition resulted in enhanced enzymatic activity.

Consistent with these biochemical data, all cryo-EM structures reveal a single, well-defined metal-binding site coordinated by three conserved cysteine residues and occupied by Zn²⁺, with no evidence for an additional iron species or other redox-active metal site.

(2) The specific activity of the enzyme should be quoted in the same units as other literature papers, so that the enzyme activity can be compared. It could be, for example, that the content of Fe (or other redox-active metal) is low, and that could then give rise to a low specific activity.

Thank you for the suggestion, we quoted the enzyme units as similar with previous report. and revised the text in in page 2.

Since the submission of our paper a new report on MsTDM has been published (Cappa et al., Protein Science 33(11), e70364). It further supports our findings. First, the reported kinetic parameters using ITC (Vmax = 0.309 μmol/s, approximately 240 nmol/min/mg; Km = 0.866 mM) are comparable to our observed (156 nmol/min/mg and 1.33 mM, respectively) in the absence of exogenous iron. Second, the optimal pH for enzymatic activity similar to that observed in our paraTDM. Third, the reported two-state unfolding behavior is consistent with our cryo-EM structural observations, in which the more dynamic subunits appear to destabilize prior to unfolding of the core domains. Based on these findings, we now propose that Zn²⁺ appears to function primarily as an organizational cofactor at the core catalytic domain (revised Scheme 1).

eLife Assessment

This manuscript reports a valuable modeling study on sequence generation in the hippocampus in a variety of behavioral contexts. The authors model context-depending decision making, and suggest that psychiatric disorders can be interpreted in terms of over or under representation of context information. The presentation is solid, and the work will interest the broad community of researchers studying cortical-hippocampal interactions and sequences.

Reviewer #2 (Public review):

[Editors' note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

Ito and Toyoizumi present a computational model of context-dependent action selection. They propose a "hippocampus" network that learns sequences based on which the agent chooses actions. The hippocampus network receives both stimulus and context information from an attractor network that learns new contexts based on experience. The model is consistent with a variety of experiments both from the rodent and the human literature such as splitter cells, lap cells, the dependence of sequence expression on behavioral statistics. Moreover, the authors suggest that psychiatric disorders can be interpreted in terms of over/under representation of context information.

My general assessment of the work is unchanged, and I still have some questions requesting methodological clarification

Strengths:

This ambitious work links diverse physiological and behavioral findings into a self-organizing neural network framework. All functional aspects of the network arise from plastic synaptic connections: Sequences, contexts, action selection. The model also nicely links ideas from reinforcement learning to a neuronally interpretable mechanisms, e.g. learning a value function from hippocampal activity.

Reviewer #3 (Public review):

Summary:

This paper develops a model to account for flexible and context-dependent behaviors, such as where the same input must generate different responses or representations depending on context. The approach is anchored in the hippocampal place cell literature. The model consists of a module X, which represents context, and a module H (hippocampus), which generates "sequences". X is a binary attractor RNN, and H appears to be a discrete binary network, which is called recurrent but seems to operate primarily in a feedforward mode. H has two types of units (those that are directly activated by context, and transition/sequence units). An input from X drives a winner-take-all activation of a single unit H_context unit, which can trigger a sequence in the H_transition units. When a new/unpredicted context arises, a new stable context in X is generated, which in turn can trigger a new sequence in H. The authors use this model to account for some experimental findings, and on a more speculative note, propose to capture key aspects of contextual processing associated with schizophrenia and autism.

Strengths:

Context-dependency is an important problem. And for this reason, there are many papers that address context-dependency - some of this work is cited. To the best of my knowledge, the approach of using an attractor network to represent and detect changes in context is novel and potentially valuable.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

Summary:

Ito and Toyoizumi present a computational model of context-dependent action selection. They propose a "hippocampus" network that learns sequences based on which the agent chooses actions. The hippocampus network receives both stimulus and context information from an attractor network that learns new contexts based on experience. The model is consistent with a variety of experiments both from the rodent and the human literature such as splitter cells, lap cells, the dependence of sequence expression on behavioral statistics. Moreover, the authors suggest that psychiatric disorders can be interpreted in terms of over/under representation of context information.

My general assessment of the work is unchanged, and I still have some questions requesting methodological clarification

Strengths:

This ambitious work links diverse physiological and behavioral findings into a self-organizing neural network framework. All functional aspects of the network arise from plastic synaptic connections: Sequences, contexts, action selection. The model also nicely links ideas from reinforcement learning to a neuronally interpretable mechanisms, e.g. learning a value function from hippocampal activity.

Weaknesses:

The presentation, particularly of the methodological aspects, needs to be heavily improved. Judgment of generality and plausibility of the results is severely hampered but is essential, particularly for the conclusions related to psychiatric disorders. In its present form, it is impossible to judge whether the claims and conclusions made are justified. Also, the lack of clarity strongly reduces the impact of the work on the field.

Thank you for pointing this out.

In the revised text, we clarified the definition of “time step” and how hippocampal neurons behaved in each time step (see individual comments below). Also, we clarified the implementation of disorder conditions in our model by indicating the exact neuron numbers of the stimulus domain in H module as below. (Other parameters were common in all conditions.)

“𝑋 consists of two domains: stimulus domain 𝑋 and context domain 𝑋. The neuron ratio in the stimulus domain over the whole neurons dim 𝑋/𝑁 is 16.7% (200 neurons) for the control condition, 2.5% (30 neurons) for the SZ condition, and 50% (600 neurons) for the ASD condition.”

Comments:

The authors have made strong efforts to improve on their description of the methods, however, it is still very hard to understand. As a result of some of their clarifications, new issues appeared that I was not able to extract in the previous version.

(1) Particularly I had problems figuring out how the individual dynamical systems are interrelated (sequences, attractor, action, learning). As I understand it now (and I still might be wrong) there is one discrete time dynamics, where in each time step one action takes place as well as the attractor and sequence dynamics are moved one step forward. Also, synaptic updates happen in every one of those time steps. The authors may verify or correct my interpretations and further improve on their description in the manuscript. It is also confusing that time in the figure panels is given in units of trials, where each trial may consist of (maybe different amounts of) multiple time steps. Are the thin horizontal red ad blue lines time steps?

Thank you for raising the confusing point.

The reviewer’s understanding is correct. In our model, at each time step the agents transition to the next environmental state (which also corresponds to the contextual state). During this step, each processing stage proceeds in order: Context selector performs attractor selection, Sequence composer performs sequence selection, followed by action selection and synaptic updates. As learning progresses and hippocampal sequences begin to predict longer futures, reducing the need for step-by-step planning. However, at least at the beginning of each task, all processes are conducted at each time step (see Fig. 1G).

In all tasks, trials are reset when the agents visit the reward sites (i.e., S4 or S5). n Fig. 2C, for example, one trial consists of three time steps (i.e., three state transitions), and the red and blue shaded regions indicate individual trials. During each time step, two types of hippocampal neurons are activated: a state-coding neuron and a transition-coding neuron. (In contrast, in X, one contextual state is active during one time step). Therefore, in Fig. 2E, two neuronal activities correspond to a single time step.

For clarification, we have revised Fig. 2 and related descriptions in the manuscript as follows.

“Here, we simplified this task by using an environment with five discrete states (S1-S5), i.e., five discrete external stimuli (Figure 2A), where agents transition to the next state at each time step.”

“Figure 2C illustrates an example of both the environmental state transition and the corresponding contextual state transition of an agent, with each trial resetting upon visiting the reward sites (S4 or S5). ”

“At each time step, one state-coding neuron and one transition-coding neuron are active in this order.”

“At each time step, the agents transition between environmental states.”

“The model’s computational dynamics are fundamentally synchronized with the environmental (behavioral) time step, and at each time step, the agents transition to the next environmental state. Upon a state transition, the agents first perform contextual state estimation by Context selector and activate a corresponding hippocampal neuron.”

(2) As a consequence of my new understanding of the model dynamics, I have become doubts about the interpretation of the attractor network as context encoding. Since the X population mainly serves to disambiguate sequence continuation, right before the action has to be taken (active for only two time steps in Figure 1C?) they could also be considered to encode task space (El-Gaby et al. 2024; doi: 10.1038/s41586-024-08145-x).

We thank the reviewer for this insightful comment.

First of all, we would like to clarify that Figure 1C shows the following process: the activity of H at time step t−1 and the external stimulus at time step t jointly provide input to X module, and the activity of X settles into a contextual state at the time step t. As explained in our response to comment (1), the activity of X remains constant during each time step.

The primary function of X module in our model is to disambiguate the environmental states defined by the external stimuli based on the history information. It is true that, in practice, whether an ongoing sequence is maintained or remapped depends on whether the observed stimulus is consistent with the predicted stimulus. However, this is a consequence of the predictive sequence obtained from scratch rather than the primary computational role of X module. In contrast, X module becomes particularly important when past experience does not uniquely determine the next state. In this situation, the agent must infer the contextual state by associating the current situation with previously experienced contexts, rather than relying solely on temporal continuity.

We also add that, in most successful cases, the contextual states learned by the agent often correspond to the hidden states of each task as a result of disambiguation. In this sense, the resulting representation may resemble a “task space” encoding, as suggested by the reviewer. However, an important aspect of our model is that the agent does not assume the existence or number of hidden states a priori. Instead, we considered the situation where the agent initially underestimates the number of contextual states, and through remapping it incrementally increases the number of contextual representations. When the number of contextual states matches the number of hidden task states, the task is typically solved.

(3) Also technically, I wonder why the authors introduce the criterion of 50(!) time steps to allow the attractor to converge, if the state of the attractor network is only relevant in one time step to choose the appropriate continuation of the sequence of actions. Is attractor dynamics important at all? What would happen if just the input and output weights to the X population are kept and the recurrent weights are set 0?

We thank the reviewer for raising this confusing point.

First, we would like to clarify that the “50 iterations” mentioned in the manuscript does not refer to 50 environmental time steps. We implemented multiple iterations of attractor updates (typically until convergence) by Context selector within each behavioral time step.

We clarify this point in the Method section as below.

“After history-based or landmark-based initialization, X iteratively updates its contextual state at the beginning of each time step according to the associative memory dynamics:”

The recurrent connectivity within the X population is essential for attractor updates. If the recurrent weights were removed (i.e., set to zero), the network would lose the ability to retrieve distinct contextual states for the same stimulus. In that case, the model would be unable to solve the context-dependent task as we showed in this manuscript.

(4) Figure 3E: How many time steps are the H cells active (red bars?) Figure 4J: What are the units of the time axis?

Thank you for pointing this out.

In Figure 3E, each time step is indicated in the X-axis ticks (i.e., each environmental state). As we explained in the comment (1), two hippocampal neurons’ activity (red bars) corresponds to each time step.

Similarly, in Figure 4J, each time step is indicated in the X-axis ticks. To better represent the results, we added descriptions of the environmental states in our model to the X-axis tick labels in Figure 4J.

We added the following texts below in Figure captions.

“The x-axis represents each time step (corresponding to environmental states), and the y-axis shows the sorted activity of H module.”

“The x-axis represents each time step (corresponding to environmental states), and the y-axis shows the decoding accuracy of each context based on hippocampal activity.”

eLife Assessment

This important study examines how chronic pain and opioid exposure interact at the cellular and molecular levels in a reward-related brain region. Using single-nucleus RNA sequencing, the authors map transcriptional changes in the rat ventral tegmental area following chronic inflammatory pain and acute morphine exposure. Notably, their convincing data support that acute morphine, not chronic pain, elicits a stress-related transcriptional response primarily in glial cells rather than neurons, challenging prevailing views of opioid action and supporting growing evidence for glucocorticoid signaling in glial responses. A limitation is the use of a single opioid dose and time point, and further discussion of these constraints would help clarify the broader implications of the findings.

Reviewer #1 (Public review):

Studies investigating global gene expression changes induced by a single morphine administration have previously been conducted in several rodent brain regions. In this work, the authors focused on the ventral tegmental area (VTA), a key structure of the reward system that has not been extensively characterized in this context. To examine genome-wide transcriptional responses, they employed single-nucleus RNA sequencing (snRNA seq), a method well-suited for profiling gene expression in VTA cells, which are otherwise difficult to isolate.

The effects of morphine on gene expression in VTA cells were assessed in naive animals, in rats exposed to chronic inflammatory pain induced by local CFA injection into the paw, and in animals subjected to both conditions. The study revealed widespread transcriptional changes following morphine administration, whereas inflammation alone produced only limited alterations-an outcome that may reflect the sensitivity or resolution of the sequencing approach used.

Further in vitro experiments conducted in multiple astrocyte models demonstrated that the increase in Fkbp5 expression observed in the VTA is unlikely to result from opioid receptor activation. Instead, the data indicate that this effect is mediated by glucocorticoid receptor stimulation. These findings suggest that the elevated Fkbp5 expression in the rat VTA represents a secondary response rather than a direct consequence of morphine exposure. Comparable transcriptional changes, as well as similar mechanistic interpretations, have been reported in previous studies examining the nucleus accumbens (NAc), reinforcing the view that glucocorticoid-dependent regulation of Fkbp5 may be a broader feature of opioid related neuroadaptations.

The present paper showed largely similar morphine-induced gene changes in both male and female VTA samples. On the other hand, several studies indicate that males and females exhibit differences in dopaminergic activation and distinct gene expression profiles in response to opioids in the reward system. Preclinical studies have found marked sex differences in Fkbp5 expression in the dorsal striatum. This issue should be better addressed both experimentally and theoretically.

Reviewer #2 (Public review):

Summary:

This study addresses an important gap in our understanding of how pain‑related neuroadaptations interact with opioid exposure at the cellular and molecular levels, particularly in terms of cell‑type-specific responses within reward‑related brain regions. By applying single‑nucleus RNA sequencing, the authors generate a comprehensive atlas of transcriptional changes in the rat VTA associated with chronic inflammatory pain and acute morphine administration.

Strengths:

Overall, the study is important, and the experiments are carefully designed and executed. The manuscript is logically structured and well written. The sample size is appropriate: nuclei were collected from 14 male and 14 female Sprague‑Dawley rats, with 6-8 animals per experimental group. The inclusion of both sexes further strengthens the study by enhancing the generalizability of the findings.

To increase translational relevance, the authors also employ a human‑derived astrocyte culture model, which helps bridge findings from rodent tissue to human‑related cellular mechanisms.

Weaknesses:

A limitation is that the study examines only a single time point after morphine administration. However, this is balanced by the use of state‑of‑the‑art , and inherently expensive, molecular tools that allow deep transcriptional profiling.

One area requiring clarification is compliance with methodological standards. The manuscript does not specify whether ARRIVE guidelines were followed, whether a power analysis was performed to justify the number of animals used, or how randomization and blinding procedures were implemented.

Reviewer #3 (Public review):

Summary:

This work examined the transcriptional response to pain induction by CFA and/or morphine treatment in rat VTA at the level of single cells. This builds on prior work using bulk-tissue RNA-seq to evaluate response to SNI pain and/or oxycodone treatment. Here, authors find few lasting gene expression changes with CFA, but a robust transcriptional response to acute morphine, particularly in non-neuronal cells, where an increase in Fkbp5 stood out. The authors validated corticosterone-induced elevations in Fkbp5 in rat glial cell culture and human astrocyte cell culture, which are blocked by the GR antagonist mifepristone and inhibition of Nr3c1, but are not independently induced by the µOR agonist DAMGO.

Strengths:

The authors started with somewhat surprising transcriptional observations and followed the science appropriately to investigate the functional relevance of one particular finding. This work is well-powered and uses state-of-the-art snRNA-seq and CRISPR-based manipulations in both rat glia and human astrocyte cell preparations to determine the functional relevance of Fkbp5-regulated transcriptional activity.

Weaknesses:

(1) It was somewhat surprising that the CFA-Morphine group was not taken at a time point when the morphine treatment was found to be behaviorally effective.

(2) The final conclusion that Nr3c1 repression reduces the response to cort is not novel or surprising, even if it is within human astrocyte culture (which is cool).

(3) This work falls short of bringing the research full circle by applying their Nr3c1-CRISPRi approach in vivo to alter behavioral response to morphine and/or pain.

eLife Assessment

This important study demonstrates the power of the UniDesign computational framework in prospectively engineering a PAM-relaxed Staphylococcus aureus Cas9 variant with editing performance comparable to evolution-derived counterparts. The authors responded promptly and thoroughly to reviewer concerns and strengthened the manuscript with additional experimental validation, providing compelling evidence through expanded biochemical characterization across multiple human cell types, comprehensive deep-sequencing analyses, and direct comparisons with established variants that illuminate the mechanistic basis of PAM specificity remodeling and Cas9 optimization. By establishing computational design as a rigorous and viable alternative to directed evolution for CRISPR systems, this work will be of broad interest to the protein engineering, genome engineering, synthetic biology, and computational protein design communities.

Reviewer #1 (Public review):

[Editors' note: The Reviewing Editor has assessed the work without involving the previous reviewers, updating the eLife Assessment accordingly. The authors did an excellent job of addressing the reviewers' comments and suggestions. The manuscript is now in line with the minor suggestions from the original reviewers, who were already enthusiastic about the first version.]

Summary:

This manuscript by Xiong and colleagues presents a compelling validation of UniDesign, a fully computational protein design framework, by using it to engineer a novel, PAM-relaxed variant of Staphylococcus aureus Cas9 (SaCas9) named KRH. The core achievement is the successful de novo generation of a high-performance nuclease (E782K/N968R/R1015H) solely through in silico modeling, without any subsequent experimental optimization or directed evolution. The authors demonstrate that KRH expands the SaCas9 PAM specificity from NNGRRT to NNNRRT, achieving genome editing and base editing efficiencies across multiple human cell types that are comparable to, and sometimes exceed, the well-known evolution-derived KKH variant. The work positions UniDesign not merely as an analytical tool, but as a powerful engine for the generative design of complex molecular functions, offering a scalable and mechanistically insightful alternative to traditional experimental screening.

Strengths:

This is an outstanding manuscript that serves as a powerful proof-of-concept for the next generation of computational protein design. The primary selling point-the raw predictive and generative power of UniDesign-is convincingly demonstrated throughout.

The manuscript shows that the tool can:

(1) successfully navigate a complex sequence landscape to identify a minimal set of three mutations (KRH) that remodel a critical protein-DNA interface;

(2) accurately model and balance the delicate interplay between specific base contacts and non-specific backbone interactions to achieve relaxed PAM specificity;

(3) deliver a final product whose performance is indistinguishable from, and in some cases superior to, a variant that required extensive wet-lab evolution.

The experimental validation is rigorous, thorough, and directly supports the computational predictions. This work will stand as a landmark study for the field, illustrating that computational design has matured to the point where it can reliably generate sophisticated tools for genome engineering.

(1) Demonstration of Generative Power:

The most significant finding is that UniDesign, without any experimental feedback, generated a variant (KRH) that matches the performance of the evolution-derived KKH. This is a remarkable achievement. The iterative design strategy-first reducing PAM bias (R1015H), then restoring binding through non-specific interactions (e.g., N968R, E782K)-is a textbook example of rational design, but it is executed entirely by the algorithm. This validates UniDesign's energy function and search algorithm as capable of capturing the subtle biophysical principles governing PAM recognition.

(2) Mechanistic Insight as a Built-in Feature:

A key advantage of UniDesign highlighted by this work is its inherent ability to provide mechanistic explanations. The computational models not only predicted which mutations would work (e.g., N968R over N968K in the KRH variant) but also why they work. The structural and energetic analyses showing the bidentate salt bridge formed by Arg968 versus the single bond formed by Lys968 (Figure 4A) is a perfect example of how the tool's output can rationalize functional differences, a level of insight that is rarely attainable from directed evolution campaigns alone.

(3) Scalability and Accessibility for Engineering:

The authors explicitly contrast UniDesign's efficiency (minutes to hours per design run) with the computational expense of methods like COMET and the experimental overhead of directed evolution. The improvements to UniDesign v1.2, specifically the mutation-count and sequence-uniqueness penalties, directly address a key challenge in computational design (generating diverse, low-energy point-mutant libraries). This positions the tool as a highly accessible and scalable platform for engineering other CRISPR systems, a point that will be of immense interest to the community.

Reviewer #2 (Public review):

Summary:

This manuscript describes the fully in silico design of a new variant of Staphylococcus aureus Cas9 (SaCas9) using an improved UniDesign workflow.

The design strategy consists of three sequential steps:

(1) Reducing positional bias at PAM position 3;<br /> (2) Restoring DNA binding through nonspecific interactions;<br /> (3) Combining individually favorable substitutions.

The overall pipeline is conceptually elegant and logically structured, and the genome-editing activity of the designed variants is comprehensively characterized. The resulting KRH variant exhibits relaxed PAM specificity, expanding the targeting range of SaCas9 across diverse cell types. Notably, the KRH variant demonstrates performance comparable to that of the evolution-derived KKH variant, underscoring the effectiveness of the proposed computational design framework.

Reviewer #3 (Public review):

Summary:

This study reports KRH, a SaCas9 variant computationally engineered via UniDesign to recognize an expanded NNNRRT PAM with substantially enhanced editing efficiency at non-canonical sites. KRH achieves genome- and base-editing efficiencies comparable to or exceeding the evolution-derived KKH variant across multiple human cell types, demonstrating that computational design can effectively remodel PAM specificity while preserving nuclease activity.

Strengths:

The research follows a clear line of reasoning, and the results appear sound. The computational design strategy presented offers a valuable alternative to directed evolution, with potential applicability beyond Cas9 engineering.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Xiong and colleagues presents a compelling validation of UniDesign, a fully computational protein design framework, by using it to engineer a novel, PAM-relaxed variant of Staphylococcus aureus Cas9 (SaCas9) named KRH. The core achievement is the successful de novo generation of a high-performance nuclease (E782K/N968R/R1015H) solely through in silico modeling, without any subsequent experimental optimization or directed evolution. The authors demonstrate that KRH expands the SaCas9 PAM specificity from NNGRRT to NNNRRT, achieving genome editing and base editing efficiencies across multiple human cell types that are comparable to, and sometimes exceed, the well-known evolution-derived KKH variant. The work positions UniDesign not merely as an analytical tool, but as a powerful engine for the generative design of complex molecular functions, offering a scalable and mechanistically insightful alternative to traditional experimental screening.

Strengths:

This is an outstanding manuscript that serves as a powerful proof-of-concept for the next generation of computational protein design. The primary selling point-the raw predictive and generative power of UniDesign-is convincingly demonstrated throughout.

The manuscript shows that the tool can:

(1) successfully navigate a complex sequence landscape to identify a minimal set of three mutations (KRH) that remodel a critical protein-DNA interface;

(2) accurately model and balance the delicate interplay between specific base contacts and non-specific backbone interactions to achieve relaxed PAM specificity;

(3) deliver a final product whose performance is indistinguishable from, and in some cases superior to, a variant that required extensive wet-lab evolution.

The experimental validation is rigorous, thorough, and directly supports the computational predictions. This work will stand as a landmark study for the field, illustrating that computational design has matured to the point where it can reliably generate sophisticated tools for genome engineering.

(1) Demonstration of Generative Power:

The most significant finding is that UniDesign, without any experimental feedback, generated a variant (KRH) that matches the performance of the evolution-derived KKH. This is a remarkable achievement. The iterative design strategy-first reducing PAM bias (R1015H), then restoring binding through non-specific interactions (e.g., N968R, E782K)-is a textbook example of rational design, but it is executed entirely by the algorithm. This validates UniDesign's energy function and search algorithm as capable of capturing the subtle biophysical principles governing PAM recognition.

(2) Mechanistic Insight as a Built-in Feature:

A key advantage of UniDesign highlighted by this work is its inherent ability to provide mechanistic explanations. The computational models not only predicted which mutations would work (e.g., N968R over N968K in the KRH variant) but also why they work. The structural and energetic analyses showing the bidentate salt bridge formed by Arg968 versus the single bond formed by Lys968 (Figure 4A) is a perfect example of how the tool's output can rationalize functional differences, a level of insight that is rarely attainable from directed evolution campaigns alone.

(3) Scalability and Accessibility for Engineering:

The authors explicitly contrast UniDesign's efficiency (minutes to hours per design run) with the computational expense of methods like COMET and the experimental overhead of directed evolution. The improvements to UniDesign v1.2, specifically the mutation-count and sequence-uniqueness penalties, directly address a key challenge in computational design (generating diverse, low-energy point-mutant libraries). This positions the tool as a highly accessible and scalable platform for engineering other CRISPR systems, a point that will be of immense interest to the community.

We sincerely thank the reviewer for the comprehensive summary and the highly positive and encouraging comments on our manuscript.

Weaknesses:

(1) Title and Abstract Emphasis:

The title and abstract are effective but could be slightly sharpened to emphasize the primary message. Consider a title like "Fully computational design of a PAM-relaxed SaCas9 variant with UniDesign demonstrates power to match directed evolution." The abstract could more explicitly state upfront that the design was achieved without any experimental iteration.

Thank you for this valuable suggestion. We have revised the title and abstract accordingly to better reflect your feedback.

(2) Figure 1, Panel M:

The data points in panel M are currently presented at a font size that makes them difficult to read, particularly the labels for the many triple-mutant variants. This density obscures the clear identification of the top-performing designs, such as the KRH variant selected for experimental validation. I recommend that the authors increase the font size of all text elements within this panel, including axis labels, tick marks, and data point labels, to improve legibility. If necessary, the panel dimensions can be adjusted or the layout reorganized to accommodate the larger text without compromising clarity. Ensuring this figure is readable is important, as it visually communicates the energetic convergence that led to the selection of KRH.

Thank you for this helpful suggestion. We have increased the font size the Figure 1M, as well as in Figure 1C and Figure 1E, to improve the readability in the revised manuscript.

(3) Generality of the Design Strategy for Other PAM Positions:

The design strategy focused on relaxing specificity at the highly constrained third position of the PAM (the guanine in NNGRRT). How transferable is this specific strategy (i.e., disrupting a key specific contact and compensating with non-specific backbone binders) to relaxing other positions in the PAM or to other Cas enzymes with different PAM-interaction architectures? A short discussion on this point would help readers understand the broader applicability of the "fine-tuning the balance" principle.

Thank you for this insightful question and suggestion. The current study builds upon our previous work on CRISPR–Cas PAM recognition modeling using UniDesign (PMID: 37078688), in which eight Cas9 proteins and two Cas12 proteins (each has a different PAM) were investigated. Our computational results demonstrated that UniDesign can effectively capture the mutual preferences between natural PAMs and native PAM-interacting amino acids (PIAAs). For example, UniDesign accurately predicted the canonical PAMs of SpCas9 and SaCas9 as NGG and NNGRRT, respectively; conversely, given their canonical PAMs, UniDesign successfully recapitulated the corresponding PIAAs in both systems.

These findings provide the foundation for the present study and motivate our selection of SaCas9 as a representative system to explore PAM relaxation, thereby further demonstrating UniDesign’s predictive power through experimental validation. Although we did not perform similar PAM relaxation designs for other Cas9 or Cas12 proteins, we believe that the UniDesign framework is broadly generalizable and can be readily extended to these systems. We have included additional discussion to clarify this point and highlight the broader applicability of our design strategy.

Reviewer #2 (Public review):

Summary:

This manuscript describes the fully in silico design of a new variant of Staphylococcus aureus Cas9 (SaCas9) using an improved UniDesign workflow.

The design strategy consists of three sequential steps:

(1) reducing positional bias at PAM position 3;

(2) restoring DNA binding through nonspecific interactions;

(3) combining individually favorable substitutions.

The overall pipeline is conceptually elegant and logically structured, and the genome-editing activity of the designed variants is comprehensively characterized. The resulting KRH variant exhibits relaxed PAM specificity, expanding the targeting range of SaCas9 across diverse cell types. Notably, the KRH variant demonstrates performance comparable to that of the evolution-derived KKH variant, underscoring the effectiveness of the proposed computational design framework.

Strengths:

The design pipeline is entirely computational and does not rely on experimental data for pretraining or iterative optimization.

We thank the reviewer for the concise and accurate summary of our manuscript.

Weaknesses:

The computationally generated KRH mutant differs from the experimentally evolved KKH variant by only a single residue, which may reflect insufficient exploration of the available sequence space.

Thank you for this insightful critique. In the present study, our strategy was not to allow UniDesign to freely explore all 27 mutable positions simultaneously, but rather to constrain the search to point mutations (e.g., double or triple mutants) within the full sequence space (approximately 20²⁷). Even with this constraint, UniDesign effectively samples a substantially large design space compared to traditional protein engineering approaches.

Through iterative design, we observed that only certain residue types became enriched at a subset of positions when identifying effective double mutants. These enriched residues were then systematically combined to generate performance-enhancing triple mutants in an automated manner. Although we ultimately selected the KRH mutant for experimental validation due to its high similarity to the known KKH variant, UniDesign also proposed additional multi-mutants that are distinct from KKH (see Figure 1M).

Reviewer #3 (Public review):

Summary:

This study reports KRH, a SaCas9 variant computationally engineered via UniDesign to recognize an expanded NNNRRT PAM with substantially enhanced editing efficiency at non-canonical sites. KRH achieves genome- and base-editing efficiencies comparable to or exceeding the evolution-derived KKH variant across multiple human cell types, demonstrating that computational design can effectively remodel PAM specificity while preserving nuclease activity.

Strengths:

The research follows a clear line of reasoning, and the results appear sound. The computational design strategy presented offers a valuable alternative to directed evolution, with potential applicability beyond Cas9 engineering.

We thank the reviewer for the concise and accurate summary of our manuscript.

Weaknesses:

The benchmarking of the UniDesign method is insufficient. How its performance compares to other protein design algorithms, whether the energy function parameters were systematically optimized, and if the design strategy can be generalized to other Cas9 orthologs or genome engineering tasks.

Thank you for this valuable critique. The present study builds upon our previous work on CRISPR–Cas PAM recognition modeling using UniDesign (PMID: 37078688), in which many of these concerns were systematically addressed. In that study, UniDesign was benchmarked against Rosetta, a well-established protein design platform, across eight Cas9 proteins and two Cas12 proteins, each recognizing distinct PAM sequences.

Our results demonstrated that UniDesign effectively captures the mutual preferences between natural PAMs and native PAM-interacting amino acids (PIAAs) across these CRISPR–Cas systems. For example, UniDesign accurately predicted the canonical PAMs of SpCas9 and SaCas9 as NGG and NNGRRT, respectively; conversely, given their canonical PAMs, UniDesign successfully recapitulated the corresponding PIAAs in both systems.

These findings provide the foundation for the present study and motivate our selection of SaCas9 as a representative system to explore PAM relaxation, thereby further demonstrating UniDesign’s predictive power through experimental validation. Although we did not perform analogous PAM relaxation designs for other Cas9 or Cas12 proteins in this work, we believe that the UniDesign framework is broadly generalizable and can be readily extended to these systems. We have incorporated additional discussion in the revised manuscript to address these points and clarify the broader applicability of our approach.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) SaCas9 is highlighted for its AAV compatibility, but the manuscript does not further discuss how the KRH variant may benefit AAV-based genome editing applications. A brief discussion on how expanded PAM compatibility could facilitate target selection in AAV-constrained therapeutic settings would strengthen the translational relevance of the work, potentially reducing the need for split-Cas9 or dual-vector strategies.

Thank you for your helpful suggestion. We have added a brief discussion in the revised manuscript highlighting how the KRH variant’s expanded PAM compatibility may enhance AAV-based genome editing applications. Specifically, this property can broaden the range of targetable genomic sites and may reduce the need for split-Cas9 or dual-vector delivery strategies in size-constrained AAV therapeutic contexts.

(2) The study shows that a fully computational workflow can recapitulate the performance of an evolution-derived variant. A short discussion comparing the scalability and practical advantages of computational design versus directed evolution for future PAM engineering would help emphasize the broader methodological significance of UniDesign.

Thank you for your valuable suggestion. We have added a brief discussion in the revised manuscript comparing the scalability and practical advantages of computational design with directed evolution for PAM engineering. Specifically, we highlight that UniDesign enables rapid and scalable exploration of sequence space without requiring iterative experimental screening, thereby offering a complementary—and in some cases more efficient—approach to directed evolution for future protein engineering applications.

(3) The noticeable variation in editing efficiency across cell types, particularly the lower activity in A549 cells. Could the authors explain why the differences in editing efficiency are so large?

Thank you for this insightful comment. We agree that the variation in editing efficiency across cell types—particularly the lower activity observed in A549 cells—warrants clarification, and we have added a corresponding discussion in the revised manuscript. We attribute this observation to two main factors. First, transfection efficiency varies substantially across cell lines; in our experiments, A549 cells exhibited lower transfection efficiency compared to HEK293T, HeLa, and U2OS cells, which likely contributes to the reduced editing efficiency. Second, the intrinsic performance of genome editing systems can differ across cellular contexts due to variations in DNA repair pathways, including chromatin accessibility and the expression levels of key repair-related genes. Importantly, despite this cell-type-dependent variability in absolute editing efficiency, the KRH variant consistently outperformed wild-type SaCas9 across all tested cell lines, underscoring the robustness and general applicability of our design.

(4) Given that the computationally generated KRH mutant differs from the experimentally evolved KKH variant by only a single residue, it would be valuable to discuss whether R968 (or saturation mutations at this site) has previously been explored experimentally, and to elaborate on strategies for further expanding the diversity of mutations identified through the computational design framework.

Thank you for your suggestion. We have added a brief discussion in the manuscript noting that, to the best of our knowledge, R968 has not been experimentally characterized prior to this study. It was identified solely through our computational design workflow, highlighting the strength of our approach.

Reviewer #3 (Recommendations for the authors):

(1) During the protein amino acid conformational sampling process in UniDesign, were nucleic acid conformational changes taken into consideration?

Thank you for this question. Nucleic acid conformational changes were not explicitly considered during the protein sequence design stage in UniDesign after the four specific PAM variants (e.g., TTAGGT, TTCGGT, TTGGGT, and TTTGGT) were defined. We consider this assumption reasonable, as the base conformations in these PAM sequences are expected to remain largely stable, with minimal structural variation due to preserved base-stacking interactions.

(2) The authors used a mutation-count penalty to control the number of mutations generated during the design process, which appears to occasionally yield results that exceed the intended limit. Is this an efficient approach? Could the count be controlled more directly by imposing constraints within the design procedure itself?

Thank you for these insightful questions. You are correct that the design process may occasionally yield variants exceeding the intended mutation limit. This occurs because the mutation-count penalty is implemented as a soft constraint, where violations incur a penalty rather than being strictly excluded. Based on our benchmarking, this strategy—combined with the duplicate-design penalty—has been effective in generating multimutant variants with mutation counts close to the desired range. However, we acknowledge that this approach may not achieve optimal efficiency. We are currently developing improved strategies in UniDesign to more directly control mutation counts by incorporating explicit constraints during the sequence simulation process, which we expect will further enhance design precision and efficiency.

(3) Is the new version of UniDesign developed specifically for the Cas9 design task in this study? What are its advantages and disadvantages compared to other state-of-the-art protein design algorithms?

Thank you for this important question. The new version of UniDesign (v1.2) was not developed specifically for Cas9 engineering. Rather, it is intended as a general framework for protein engineering tasks that focus on introducing point mutations to improve protein properties, as opposed to de novo design. Compared to current state-of-the-art protein design methods—many of which are deep learning–based—UniDesign offers distinct advantages and limitations. Deep learning approaches are often highly efficient and powerful but may lack interpretability in their predictions. In contrast, UniDesign is a well-benchmarked, lightweight, physics-based method that provides greater interpretability, allowing users to better understand the underlying basis of the design decisions. On the other hand, a limitation of UniDesign is that it is less straightforward to incorporate experimental feedback for iterative refinement, such as fine-tuning the scoring function for specific design tasks.

(4) The study employed a three-round design process to obtain the mutants. Is there a conformational correlation between the mutation sites identified in these three rounds? Could this have been accomplished in a single computational run instead of three separate calculations?

Thank you for these insightful questions. We adopted a multi-round design strategy for SaCas9 PAM relaxation because this task inherently involves multi-objective optimization: enhancing PAM compatibility—particularly relaxing base recognition at the third PAM position—while preserving editing activity comparable to wild-type SaCas9. In our view, identifying the key mutations (e.g., E782K, N968R, and R1015H) in a single UniDesign run would be highly challenging due to competing energetic requirements. In the first round, R1015H emerged from single-site mutational scanning as the most favorable PAM-relaxing mutation based on its minimal MAD score. However, this mutation also significantly increased the binding energy relative to wild-type SaCas9 with its native PAM, suggesting a likely reduction in editing activity due to weakened binding. To address this, the second round focused on compensatory mutations. Variants such as E782K and N968R (along with several additional candidates) were identified in the context of R1015H to reduce binding energy and partially restore affinity. In the third round, we further combined compatible mutations from the second round, resulting in variants that more effectively lowered binding energy and restored it to levels comparable to wild-type SaCas9 with its native PAM. Notably, the design objectives in rounds one and two drive binding energy in opposite directions, making it unlikely that all key mutations could be identified simultaneously in a single run. During the design process, we also observed conformational correlations among mutation sites. For example, R1015H can form hydrogen-bonding interactions with residue E993, and we observed multiple alternative mutations at position 993 (e.g., E993S, E993P, E993A, E993G, E993K, and E993R), suggesting local structural coupling between these positions.

(5) In Figure 4D, for the FANCF-1 site, there appears to be a noticeable difference in editing efficiency between KKH-ABE and KRH-ABE. Is this difference statistically significant? If so, please provide an explanation for this observation.

Thank you for this question. For the FANCF-1 site shown in Figure 4D, we performed statistical analyses and found that the differences in editing efficiency between KKH-ABE and KRH-ABE are not statistically significant: P(A4) = 0.1239, P(A10) = 0.0671, P(A12) = 0.0942, and P(A13) = 0.1349 (two-tailed unpaired Student’s t-test). These results indicate that KRH-ABE and KKH-ABE exhibit comparable editing efficiencies at this site, supporting our overall conclusion that the computationally designed KRH variant achieves performance on par with the KKH variant.

(6) Does the evolutionary term within the UniDesign scoring function bias the designed sequences towards pre-existing protein features?

Thank you for this question. In this study, as well as in our previous work on Cas9 PAM recognition modeling (PMID: 37078688), the evolutionary term in the UniDesign scoring function was completely disabled. Therefore, it does not introduce any bias toward pre-existing protein features in the designed sequences.

eLife Assessment

This paper presents an important theory and analysis of the role of neurogenesis and inhibitory plasticity in the drift of neural representations in the olfactory system. For one of the findings, regarding the impact of neurogenesis on the drift, the evidence remains incomplete. The reason lies in the differences in variability/drift of the mitral/tufted cell responses observed in the model compared to experimental observations, where these responses remain stable over extended time scales.

Reviewer #1 (Public review):

Summary:

The authors build a network model of the olfactory bulb and the piriform cortex and use it to run simulations and test their hypotheses. Given the the model's settings, the authors observe drift across days in the responses to the same odors of both the mitral/tufted cells, as well as of piriform cortex neurons. When representing the M/T and PCx responses within a lower dimensional space, the apparent drift is more prominent in the PCx, while the M/T responses appear in comparison more stable. The authors further note that introducing spike-time dependent plasticity (STDP) at bulb synapses involving abGCs slows down the drift in the PCx representations, and further link this to the observation that repeated exposure to the same odorant slows down drift in the piriform cortex.

The model is clearly explained and relies on several assumptions and observations: 1) random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity and random piriform to bulb connectivity; 3) higher dimensionality of piriform cortex representations compared to M/T responses which enables superior decoding of odor identity in the piriform cortex; 2) spike time dependent plasticity (STDP) at synapses involving the abGCs.

The authors address an open topical problem and model is elegant in its simplicity. The authors addressed many of my concerns by plotting new analyses and by adding clarifying statements and discussion points, as well as testable predictions to the revised manuscript. In the revised manuscript, a few points remain unclear and I am listing them below for further potential discussion.

(1) Given the large in response (variability) across trials reported by Shani-Narkiss, Kay & Laurent - the question remains open: what fraction of the variability in response across days can be really accounted by adult born neurogenesis (the main topic of this study) vs. other mechanisms. I think the answer to this question is key for interpreting the results presented by the authors on the impact of adult neurogenesis on changes of mitral cell responses. Unfortunately, I could not find the answer in the revised version of the manuscript.

(2) Yamada indeed reported a "drastic reorganization of ensemble odor representation" in their manuscript (Figure 3D), but my understanding is that this was observed in the context of passive exposure to the same odor across several days in a row. This does not appear to contradict the findings of Kato et al., 2012 that when an odor is presented seldom, across days the mitral cell responses are stable. Also, data from Yamada et al. appears to show some degree of overall sparsening of odor responses in mitral cells at least at the level of a decrease in response amplitude between day 1 to day 7 of repeated passive exposure (Figure 3A, Yamada et al., 2017).

(3) There was mistake on my part on one of the papers referenced with respect to random vs. structured projections from the olfactory bulb to the piriform cortex. The one I was referring to is Chen et al., Cell, 2022 (not Chae et al., Neuron, 2022). The authors discussed the implications from the latter, while I was commenting in fact on the findings from Chen et al., 2022. This study identified structured projections of individual mitral cells along the A-P axis of the piriform cortex in conjunction with collaterals to specific subsets of extra-piriform target regions.

Reviewer #3 (Public review):

Summary

The authors set out to explore the potential relationship between adult neurogenesis of inhibitory granule cells in the olfactory bulb and cumulative changes over days in odor-evoked spiking activity (representational drift) in the olfactory stream. They developed a richly detailed spiking neuronal network model based on Izhikevich (2003), allowing them to capture the diversity of spiking behaviors of multiple neuron types within the olfactory system. This model recapitulates the circuit organization of both the main olfactory bulb (MOB) and the piriform cortex (PCx), including connections between the two (both feedforward and corticofugal). Adult neurogenesis was captured by shuffling the weights of the model's granule cells, preserving the distribution of synaptic weights. Shuffling of granule cell connectivity resulted in cumulative changes in stimulus-evoked spiking of the model's M/T cells. Individual M/T cell tuning changed with time, and ensemble correlations dropped sharply over the temporal interval examined (long enough that almost all granule cells in the model had shuffled their weights). Interestingly, these changes in responsiveness did not disrupt low-dimensional stability of olfactory representations: when projected into a low-dimensional subspace, population vector correlations in this subspace remained elevated across the temporal interval examined. Importantly, in the model's downstream piriform layer this was not the case. There, shuffled GC connectivity in the bulb resulted in a complete shift in piriform odor coding, including for low-dimensional projections. This is in contrast to what the model exhibited in the M/T input layer. Interestingly, these changes in PCx extended to the geometrical structure of the odor representations themselves. Finally, the authors examined the effect of experience on representational drift. Using an STDP rule, they allowed the inputs to and outputs from adult-born granule cells to change during repeated presentations of the same odor. This stabilized stimulus-evoked activity in the model's piriform layer.

Strengths

This paper suggests a link between adult neurogenesis in the olfactory bulb and representational drift in the piriform cortex. Using an elegant spiking network that faithfully recapitulates the basic physiological properties of the olfactory stream, the authors tackle a question of longstanding interest in a creative and interesting manner. As a purely theoretical study of drift, this paper presents important insights: synaptic turnover of recurrent inhibitory input can destabilize stimulus-evoked activity, but only to a degree, as representations in the bulb (the model's recurrent input layer) retain their basic geometrical form. However, this destabilized input results in profound drift in the model's second (piriform) layer, where both the tuning of individual neurons and the layer's overall functional geometry are restructured. This is a useful and important idea in the drift field and to my knowledge is novel. The bulb is not the only setting where inhibitory synapses exhibit turnover (whether through neurogenesis or synaptic dynamics), and so this exploration of the consequences of such plasticity on drift is valuable. The authors also elegantly explore a potential mechanism to stabilize representations through experience, using an STDP rule specific to the inhibitory neurons in the input layer. This has an interesting parallel with other recent theoretical work on drift in the piriform (Morales et al., 2025 PNAS), in which STDP in the piriform layer was also shown to stabilize stimulus representations there. It is fascinating to see that this same rule also stabilizes piriform representations when implemented in the bulb's granule cells.

The authors also provide a thoughtful discussion regarding differential roles of mitral and tufted cells in drift in piriform and AON and potential roles of neurogenesis in archicortex.

In general, this paper puts an important and much-needed spotlight on the role of neurogenesis and inhibitory plasticity in drift. In this light, it is a valuable and exciting contribution to the drift conversation.

Comments on revisions:

I appreciate the substantial revisions the authors have made to the manuscript. The paper is clearly improved and addresses an important and timely question: the relationship between adult neurogenesis and drift. In particular, the effort to link adult neurogenesis in the olfactory bulb to the long-term stability of odor representations downstream is valuable, and the modeling provides useful mechanistic intuition about how inhibitory circuit remodeling could influence representational drift across layers.

That said, I remain concerned that the manuscript, as currently framed, risks giving readers the incorrect impression that experimental work has established progressive, time-dependent drift in the odor tuning of olfactory bulb neurons. Experimental studies do show that ongoing experience with a set of odors can profoundly alter bulbar responses to those odors, but longitudinal measurements in which the tested odors are not repeatedly presented between sessions have instead emphasized remarkable stability of mitral/tufted tuning over days to months across multiple groups. I also think it would strengthen the manuscript to avoid anchoring the empirical comparison too heavily on a single paradigm (Yamada et al., 2017). The experimental literature spans multiple regimes, including daily odor exposure with ongoing experience and longitudinal measurements in which the tested odors are not repeatedly presented between sessions, and these regimes can yield qualitatively different degrees of reorganization. Situating the model explicitly within this broader landscape, rather than emphasizing one dataset, would make the interpretation clearer and prevent readers from overgeneralizing the Yamada findings to baseline bulbar stability. This distinction is especially important because it contrasts with what has been reported in piriform cortex, where representational drift is observed even in the absence of ongoing experience with a given odor set, and where repeated daily encounters with the same odors can slow or arrest that drift.

Author response:

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

We thank the editor and reviewers for their thoughtful and constructive feedback. We appreciate that all reviewers recognized the value of our study in linking adult neurogenesis and synaptic plasticity to representational drift in the olfactory system. They described the model as elegant and well-motivated, and agreed that it provides new theoretical insight into how stability and adaptability can coexist in sensory representations. The reviewers also identified areas where our manuscript could be strengthened, and as outlined in our revision plan we have:

(1) Refined our description of mitral/tufted cell stability and expand on within-session and across-day variability.

(2) Substantially expanded the Discussion to compare our modeling assumptions with experimental findings and recent anatomical evidence. Additionally, we have included the limitations of the study and areas for future investigation.

(3) Included a clearer description of the STDP implementation, plastic synapses, and their functional effects.

(4) Add a short section outlining model-based predictions that can guide future experiments. We also made minor textual edits to improve precision and flow, including citing prior conceptual work and clarifying model procedures.

These changes have strengthened both the conceptual framing and technical clarity of the paper. We are grateful for the reviewers’ careful reading and valuable suggestions.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors build a network model of the olfactory bulb and the piriform cortex and use it to run simulations and test their hypotheses. Given the model's settings, the authors observe drift across days in the responses to the same odors of both the mitral/tufted cells, as well as of piriform cortex neurons. When representing the M/T and PCx responses within a lower-dimensional space, the apparent drift is more prominent in the PCx, while the M/T responses appear in comparison more stable. The authors further note that introducing spike-time dependent plasticity (STDP) at bulb synapses involving abGCs slows down the drift in the PCx representations, and further link this to the observation that repeated exposure to the same odorant slows down drift in the piriform cortex.

The model is clearly explained and relies on several assumptions and observations:

(1) Random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity, and random piriform to bulb connectivity.

(2) Higher dimensionality of piriform cortex representations compared to M/T responses, which enables superior decoding of odor identity in the piriform cortex.

(3) Spike time-dependent plasticity (STDP) at synapses involving the abGCs.

The authors address an open topical problem, and the model is elegant in its simplicity. I have however, several major concerns with the hypotheses underlying the model and with its biological plausibility.

Concerns:

(1) In their model, the authors propose that MTC remain stable at the population level, despite changes in individual MTC responses.

The authors cite several experimental studies to support their claims that individual MTC responses to the same odors change (some increase, some decrease) across days. Interpreting the results of these studies must, however, take into account the variability of M/T responses across odor presentation repeats within the same session vs. across sessions. In the Shani-Narkiss et al., Frontiers in Neural Circuits, 2023 study referenced, a large fraction of the variability across days in M/T responses is also observed across repeats to the same odorant in the same session (Shani-Narkiss et al., Figure 4), while the authors have M/T responses in the same session that are highly reproducible. This is an important point to consider and address, since it constrains how much of the variability in M/T responses can be attributed to adult neurogenesis in the olfactory bulb versus to other networks' inhibitory mechanisms, which do not rely on neurogenesis. In the authors' model, the variability in M/T responses observed across days emerges as a result of adult-born neurogenesis, which does not need to be the main source of variability observed in imaging experiments (Shani-Narkiss et al., Figure 4).

We agree with the reviewer and believe this is a critical discussion point. Indeed, both in Shani-Narkiss et al, Kay and Laurent, 1999, and in our lab, we observe trial-to-trial variability that occurs in the same recording session; as the reviewer correctly points out, this cannot be due to neurogenesis. These fluctuations may be trial to-trial noise, or reflect dynamics associated with other behaviors such as running (Chockanathan, et al. 2021) and decision making (Kay and Laurent, 1999). There is growing repertoire of literature showing that neural variability in early sensory coding appears to depend on behavioral fluctuations and internal states (Niell and Stryker for example). This variability that happens within a session in the Shani-Narkiss et al work may reflect some of these behaviorally relevant features of early olfactory coding, something that our model cannot account for. This is an excellent discussion point and we have included text (line 153-157, and line 321-330) in the manuscript to note this aspect of the data and how one can think of it in the context of our results.

Another study (Kato et al., Neuron, 2012, Figure 4) reported that mitral cell responses to odors experienced repeatedly across 7 days tend to sparsen and decrease in amplitude systematically, while mitral cell responses to the same odor on day 1 vs. day 7 when the odor is not presented repeatedly in between seem less affected (although the authors also reported a decrease in the CI for this condition). As such, Kato et al. mostly report decreases in mitral cell odor responses with repeated odor exposure at both the individual and population level, and not so much increases and decreases in the individual mitral cell responses, and stability at the population level.

Thank you for raising this important point regarding the findings of Kato et al. (2012). We agree that their results suggest increased sparsening and stability in M/T cell odor responses with repeated exposure. However, as noted in Yamada et al. (2017), the experimental literature on this question remains mixed. Yamada and colleagues reported a “drastic reorganization of ensemble odor representation” across days and emphasized that “sensory experience does not necessarily cause a major sparsening of the odor response,” explicitly contrasting their findings with those of Kato et al. (2012).

Our model captures the dynamics observed in Yamada et al. (2017), providing a mechanistic explanation for how significant reorganization can emerge in M/T ensembles despite stable low-dimensional population structure. In both Yamada et al (2017) and Kato et al (2012) the investigators have nuanced differences in experimental design (method of head fixation, behavioral paradigm used, training etc.), all of which are known to affect olfactory responses and therefore the degree of sparsity and overlap in population codes. Our model does not include any of these behavioral features that may differentially engage the olfactory circuit and thus affect population responses. Notably, in previous work, we highlight how even simple changes to top down feedback that reflect one phenomenological manipulation to functional connectivity in the olfactory circuit could have disparate effects on the degree of sparsity in neural representations over time whereby this manipulation would be activated by some behavior broadly. In our current model, there is no behavior that would allow us to study the critical features of the neural activity code in the M/T cells. Instead we focus on one specific aspect, adult neurogenesis which we can explicitly manipulate and affect in a biologically meaningful way. The review’s point however is well taken and important, and we have added text to the Discussion (line 336-344) to highlight the differing experimental outcomes and to clarify how our model aligns with the Yamada et al. results.

(2) In Figure 1, a set of GCs is killed off, and new GCs are integrated in the network as abGC. Following the elimination of 10% of GCs in the network, new cells are added and randomly assigned synaptic weights between these abGCs and MTC, GCs, SACs, and top-down projections from PCx. This is done for 11 days, during which time all GCs have gone through adult neurogenesis.

Is the authors' assumption here that across the 11 days, all GCs are being replaced? This seems to depart from the known biology of the olfactory bulb granule cells, i.e., GCs survive for a large fraction of the animal's life.

Thank you for raising this important point regarding the lifespan of granule cells (GCs). We agree that developmentally born GCs are not fully replaced. Indeed, multiple studies indicate that some developmentally born GCs can survive for very long periods, up to 18-24 months, essentially the lifetime of the animal (Kaplan, 1985; Petreanu & Alvarez-Buylla, 2002). However, the fraction of total GCs that such long lived GCs constitute remains an open question, in part because of challenges to measure the lifetime survival of newborn neurons. What there is consensus on is the significant size of the granule-cell population undergoing continuous turnover through adult neurogenesis (reviewed in Lepousez et al., 2013).

We should clarify that we do not assume that 100% of the granule cell population turns over in an 11 day period. We use “day” to represent a static epoch over which we can implement plasticity rules across two time scales. Critically, we also randomize the turnover treating every cell in the GC population as equally likely to be replaced. Prior experimental evidence suggests that some GCs are more likely to persist (possibly as a result of experience, Magavi et al., 2005) which may in some regards make our result on stabilization following repeated sensory exposure more dramatic (as the GCs that show the largest change following STDP may also be the ones that are the most stable, and therefore least likely to turnover). We do not include this in our model as we could not identify a framework for “selecting” which GCs would persist that would not be tautological. The point the reviewer raises is critical, and a discussion of these points is warranted - which we now include in the manuscript (line 352-361).

Additionally, there is some evidence that behaviors, such as novelty, can increase the rate of adult neurogenesis (Kamimura et al., 2022, H.van Praag et al.,1999, Gheusi and Lledo., 2014) , suggesting a complex reciprocal relationship between the mechanisms that generate the cells shaping how olfactory stimuli are encoded for and the encoding process itself; our model also does not include any of these dynamic features which represent an additional layer of complexity, which may further provide an intermediate time scale, one of behavioral selection and action, that is slower than the milliseconds on which spike time dependent plasticity happens, but faster than the time scale of neurogenesis. We include this point in the discussion also (line 352-361). 

Our 11-day simulation however is designed to uncover how plasticity across multiple timescales (STDP and adult neurogenesis) at the network level shapes odor representations as multiple rounds of GC turnover occur. Changing the timescale and magnitude replacement in the simulations (either in terms of days or percent cells replaced) would affect the degree to which drift happens, but not phenomenon. Additionally, the representational structure in our model at intermediate time points (e.g., days 8~10) would correspond well to scenarios in which some fraction of developmentally born GCs persists in the circuit. Thus, our simulations span a range of possible empirical regimes, from high turnover to partial preservation. We have added discussion to the revised manuscript (line 352-361) clarifying this point and acknowledging the biological heterogeneity in GC lifespans.

(3) The authors' model relies on several key assumptions: random projections of MTC from the olfactory bulb to the piriform cortex, random intra-piriform connectivity, and random piriform to bulb connectivity. These assumptions are not necessarily accurate, as recent work revealed structure in the projections from the olfactory bulb to the piriform cortex and structure within the piriform cortex connectivity itself (Fink et al., bioRxiv, 2025; Chae et al., Cell, 2022; Zeppilli et al., eLife, 2021).

How do the results of the model relating adult neurogenesis in the bulb to drift in the piriform cortex representations change when considering an alternative scenario in which the olfactory bulb to piriform and intra-piriform connectivity is not fully distributed and indistinguishable from random, but rather is structured?

Thank you for pointing us to these important studies. We fully agree with the reviewer that the structure of the olfactory system might not be purely random, but we do not believe these papers contradict the level of abstraction used in our model.

Zeppilli et al. (2021) map molecularly defined projection neuron subtypes and their preferential targeting of different cortical and subcortical regions, but they do not report any fine-scale topographic organization of bulb → piriform connectivity that would contradict a view of randomly distributed input to piriform cortex. Studies from our lab using retrograde tracers in the blub show some spatial clustering of piriform cortical neurons whose axons project to the bulb (Padmanabhan et al., 2016, 2019), but these studies do not identify any “functional organization” or structure. Chae et al., (2022) focus on distinct long-range functional loops (mitral ↔ piriform vs tufted ↔ AON) and the differential role of cortical feedback, but again, at the level of cortical regions rather than individual cells and connectivity. Notably, our model does not consider AON.

Finally, Fink et al. (2025) reports a “like-to-like” excitatory connectivity motif within the piriform cortex and an experience-dependent reorganization of inhibitory synapses. As the authors note, “... this like-to-like motif is unlikely to reflect common input from the olfactory bulb”, so it does not conflict with our assumption of broadly random bulb → piriform input. This “like-to-like” motif is reflected in our model by wiring a certain subpopulation of piriform cells. On the other hand, we agree that the experience dependent changes in inhibitory connectivity within PCx are highly relevant for learning related plasticity but fall outside the scope of our study. We intentionally omitted piriform plasticity to isolate the contributions of adult neurogenesis in the bulb and plasticity acting on adult-born granule cells. But incorporating such cortical plasticity is an important direction for future work. We added a discussion (line 395-405) on this important point raised by the reviewer in the revised manuscript.

(4) I didn't understand the logic of the low-dimensional space analysis for M/T cells and piriform cortex neurons (Figures 2 & 3). In the authors' model, the full-ensemble M/T responses are reorganized over time, presumably due to the adult-born neurogenesis. Analyzing a lower-dimensional projection of the ensemble trajectories reveals a lower degree of re-organization. This is the same for the piriform cortex, but relatively, the piriform ensembles displayed in a low-dimensional embedding appear to drift more compared to the M/T ensembles.

This analysis triggers a few questions: which representation is relevant for the brain function - the high or the low-dimensional projection? What fraction of response variance is included in the low-dimensional space analysis? How did the authors decide the low-dimensional cut-off? Why does STDP cause more drift in piriform cortex ensembles vs. M/T ensembles? Is this because of the assumed higher dimensionality of the piriform cortex representations compared to the mitral cells?

Thank you for these thoughtful questions. We clarify the logic and purpose of the low-dimensional analyses and address each point below.

(1) Which representation is relevant for brain function, the high-dimensional or low-dimensional one?

We believe both representations are meaningful, with each capturing different aspects of the neural code. The high-dimensional activity reflects the full variability of individual cell responses, while the low-dimensional projection captures the dominant population level components that downstream areas are most likely to use for readout. We found that the low-dimensional representations are more stable in the bulb than in PCx, suggesting that information is used differentially between the two areas. The bulb provides a stable, sensory-anchored population code that reliably represents odor identity over time, consistent with both electrophysiological and behavioral studies (Nagayama et al., 2004, Chen et al., 2009, Davison and Katz, 2007, Cavaretta et al., 2018). This is consistent with its role as the first stage of information processing in the olfactory system which provides faithful representations that downstream circuits receive. The piriform cortex, by contrast, transforms this stable input into a more flexible representation. Drift in its low-dimensional space may reflect ongoing plasticity (Schoonover et al., Nature, 2021), integration of contextual signals, or higherdimensional computations characteristic of PCx (Fink et al., bioRxiv, 2025), suggesting its role more as an associative cortex instead of a pure sensory cortex.

(2) What fraction of variance is included in the low-dimensional space, and how was the cutoff chosen?

In our simulations, these PCs captured the majority of variance relevant for odor identity (~60–70% for M/T cells and ~55–65% for piriform cortex). We now report these fractions explicitly in Methods (line 937-939).

(3) Why does STDP cause more drift in piriform-cortex ensembles than in M/T ensembles? Does this reflect higher dimensionality in piriform cortex?

In our model, STDP does not cause more drift in PCx. It actually reduces drift and stabilizes PCx representations relative to the condition without STDP (as shown in Fig. 4C2). STDP has a much smaller effect in the bulb because: (1) M/T cells continue to receive stable odor input from the glomeruli and (2) the low-dimensional M/T representation is already stable even without plasticity. We have edited the manuscript to reiterate this point in both the results and discussion.

The reviewer is correct that the piriform cortex naturally exhibits more drift than the bulb, and their comment that this is due to its substantially higher representational dimensionality is spot on. The PCx contains many more neurons, receives highly divergent OB → PCx inputs, and has dense recurrent connectivity, all of which create many more degrees of freedom through which representations can drift. Additionally, because individual PCx neurons are sampling from a substantially more diverse combinatorial space of inputs (include feedback to piriform from an array of regions, Illig, 2005, Majak et al., 2004, Chapuis et al., 2013), the “dimensionality” of the population code is likely higher dimensional. While STDP stabilizes the dimensions of the PCx representation that are reinforced during plasticity, due to the large number of orthogonal dimensions available, some residual drift remains. Additionally, as the reviewer notes, there are some forms of plasticity, such as inhibitory plasticity in PCx that are not included in the model, that may also have an impact on both the representations, and the underlying dimensionality of those representations. We include these points in the discussion (line 381-394).

(5) Could the authors comment whether STDP at abGC synapses and its impact on decreasing drift represent a new insight, and also put it into context? Several studies (e.g., Lledo, Murthy, Komiyama groups) reported that abGC integrates in the network in an activity-dependent manner, and not randomly, and as such stabilizes the active neuronal responses, which is consistent with the authors' report.

Related, I couldn't find through the manuscript which synapses involving abGCs they focus on, or what is the relative contribution of the various plastic synapses shown in the cartoon from Figure 4 A1 (circles and triangles).

We thank the reviewer for raising this question. As the reviewer pointed out, several studies have shown that abGCs integrate into the bulb circuit in an activity dependent manner. They preferentially form synapses onto mitral/tufted cells that respond to behaviorally important odors, this “selection of surviving cells” is not included in our model. Instead, we use STDP at the synaptic level. This is of course not analogous, but provides a computational framework wherein the selection of surviving abGCs could be incorporated in future studies. It is perhaps notable that in our large scale simulations, synaptic changes at the population level may reflect some of this activity-dependent selection.

To that end, our model provides a new insight and suggests a broader function for adult neurogenesis. For example, when certain odors are reinforced in an activity dependent manner, abGCs born during that period may stabilize the circuits that respond to those odors. The resulting reduction of drift would help keep the representation of those odors stable over time, even while other parts of the circuit continue to change. We now highlight this idea in the Discussion (line 366-373).

For the second part of the question: in our model, STDP acts on two sets of connections. It applies to the synapses onto abGCs from M/T cells, GC/SAC cells, and PCx neurons. It also applies to the synapses that abGCs project to, including those onto M/T cells and GC/SAC cells. We have clarified this in the revised Methods (line 10011004).

(6) The study would be strengthened, in my opinion, by including specific testable predictions that the authors' models make, which can be further food for thought for experimentalists.

How does suppression of adult-born neurogenesis in the OB impact the stability of mitral cell odor responses? How about piriform cortex ensembles?

We appreciate the reviewer’s suggestion and formalize the following two predictions from our model:

Prediction 1: Suppressing adult neurogenesis will reduce spontaneous representational drift in the PCx. Increasing spike-timing-dependent plasticity during periods of experience with a specific odor will selectively stabilize representations of that odor.

Prediction 2: Adult neurogenesis will not affect AON representations of odor identity or concentration in the same way that PCx representations are altered and drift.

We include these two ideas in the discussion as experimentally testable predictions.

Reviewer #2 (Public review):

Summary:

The authors address a critical problem in olfactory coding. It has long been known that adult neurogenesis, specifically in the form of adult-born granule cells that embed into the existing inhibitory networks on the olfactory bulb, can potentially alter the responses of Mitral/Tufted neurons that project activity to the Piriform Cortex and to other areas of the brain. Fundamentally, it would seem that these granule cells could alter the stability of neural codes in the OB over time. The authors develop a spiking network model to explore how stability can be achieved both in the OB over time and in the PC, which receives inputs. The model recapitulates published activity recordings of M/T cells and shows how activity in different M/T cells from the same glomerulus shifts over time in ways that, in spite of the shift, preserve population/glomerular level codes. However, these different M/T cells fan out onto different pyramidal cells of the PC, which gives rise to instability at that level. STDP then, is necessary to maintain stability at the PC level as long as odor environments remain constant. These results may also apply to a similar neurogenesis-based change in the Dentate Gyrus, which generates instability in CA1/3 regions of the hippocampus

Strengths:

A robust network model that untangles important, seemingly contradictory mechanisms that underlie olfactory coding.

Weaknesses:

The work is a significant contribution to understanding olfactory coding. But the manuscript would benefit from a brief discussion of why neurogenesis occurs in the first place - e.g., injury, ongoing needs for plasticity, and adapting to turnover of ORNs. There is literature on this topic. It seems counterintuitive to have a process in the MOB (and for that matter in the DG) that potentially disrupts the ability to generate stable codes both in the MOB and PC, and in particular a disruption that requires two different mechanisms - multiple M/T cells per glomerulus in the MOB and STDP in the PC - to counteract.

We appreciate the reviewer’s suggestion and added discussion on this point in the revised manuscript (line 431-435).

Given that neurogenesis has an important function, and a mechanism is in place to compensate for it in the MOB, why would it then be disrupted in fan-out projections to the PC? The answer may lie in the need for fan-out projections so that pyramidal neurons in the PC can combinatorially represent many different inputs from the MOB. So something like STDP would be needed to maintain stability in the face of the need for this coding strategy.

This kind of discussion, or something like it, would help readers understand why these mechanisms occur in the first place. It is interesting that PC stability requires that odor environments be stable, and that this stability drives PC representational stability. This result suggests experimental work to test this hypothesis. As such, it is a novel outcome of the research.

We agree with the reviewer. The fan-out from the bulb to the piriform cortex is essential for the combinatorial coding that allows PCx neurons to represent many odor features and mixtures. This architecture gives the piriform cortex great coding capacity, but it also makes the system sensitive to small changes in its inputs. As a result, drift that originates in the bulb can spread more easily in PCx. A stabilizing mechanism is therefore needed downstream. In our model, STDP provides this stabilization by reinforcing the dimensions that carry meaningful odor structure. This allows the piriform cortex to keep a stable population code even when its inputs change over time. Neurogenesis supplies the flexibility, the fan-out supplies the expressive power, and STDP supplies the stability. All three elements work together to support a system that must recognize odors reliably while still adapting to new sensory experiences. We have added discussion on this point in the revised manuscript (line 395-405).

Reviewer #3 (Public review):

Summary

The authors set out to explore the potential relationship between adult neurogenesis of inhibitory granule cells in the olfactory bulb and cumulative changes over days in odorevoked spiking activity (representational drift) in the olfactory stream. They developed a richly detailed spiking neuronal network model based on Izhikevich (2003), allowing them to capture the diversity of spiking behaviors of multiple neuron types within the olfactory system. This model recapitulates the circuit organization of both the main olfactory bulb (MOB) and the piriform cortex (PCx), including connections between the two (both feedforward and corticofugal). Adult neurogenesis was captured by shuffling the weights of the model's granule cells, preserving the distribution of synaptic weights. Shuffling of granule cell connectivity resulted in cumulative changes in stimulus-evoked spiking of the model's M/T cells. Individual M/T cell tuning changed with time, and ensemble correlations dropped sharply over the temporal interval examined (long enough that almost all granule cells in the model had shuffled their weights).

Interestingly, these changes in responsiveness did not disrupt low-dimensional stability of olfactory representations: when projected into a low-dimensional subspace, population vector correlations in this subspace remained elevated across the temporal interval examined. Importantly, in the model's downstream piriform layer, this was not the case. There, shuffled GC connectivity in the bulb resulted in a complete shift in piriform odor coding, including for low-dimensional projections. This is in contrast to what the model exhibited in the M/T input layer. Interestingly, these changes in PCx extended to the geometrical structure of the odor representations themselves. Finally, the authors examined the effect of experience on representational drift. Using an STDP rule, they allowed the inputs to and outputs from adult-born granule cells to change during repeated presentations of the same odor. This stabilized stimulus-evoked activity in the model's piriform layer.

Strengths

This paper suggests a link between adult neurogenesis in the olfactory bulb and representational drift in the piriform cortex. Using an elegant spiking network that faithfully recapitulates the basic physiological properties of the olfactory stream, the authors tackle a question of longstanding interest in a creative and interesting manner. As a purely theoretical study of drift, this paper presents important insights: synaptic turnover of recurrent inhibitory input can destabilize stimulus-evoked activity, but only to a degree, as representations in the bulb (the model's recurrent input layer) retain their basic geometrical form. However, this destabilized input results in profound drift in the model's second (piriform) layer, where both the tuning of individual neurons and the layer's overall functional geometry are restructured. This is a useful and important idea in the drift field, and to my knowledge, it is novel. The bulb is not the only setting where inhibitory synapses exhibit turnover (whether through neurogenesis or synaptic dynamics), and so this exploration of the consequences of such plasticity on drift is valuable. The authors also elegantly explore a potential mechanism to stabilize representations through experience, using an STDP rule specific to the inhibitory neurons in the input layer. This has an interesting parallel with other recent theoretical work on drift in the piriform (Morales et al., 2025 PNAS), in which STDP in the piriform layer was also shown to stabilize stimulus representations there. It is fascinating to see that this same rule also stabilizes piriform representations when implemented in the bulb's granule cells.

The authors also provide a thoughtful discussion regarding the differential roles of mitral and tufted cells in drift in piriform and AON and the potential roles of neurogenesis in archicortex.

In general, this paper puts an important and much-needed spotlight on the role of neurogenesis and inhibitory plasticity in drift. In this light, it is a valuable and exciting contribution to the drift conversation.

We appreciate the reviewer’s comment and thank them for their thoughtful feedback.

Weaknesses

I have one major, general concern that I think must be addressed to permit proper interpretation of the results.

I worry that the authors' model may confuse thinking on drift in the olfactory system, because of differences in the behavior of their model from known features of the olfactory bulb. In their model, the tuning of individual bulbar neurons drifts over time.

This is inconsistent with the experimental literature on the stability of odor-evoked activity in the olfactory bulb.

In a foundational paper, Bhalla & Bower (1997) recorded from mitral and tufted cells in the olfactory bulb of freely moving rats and measured the odor tuning of well-isolated single units across a five-day interval. They found that the tuning of a single cell was quite variable within a day, across trials, but that this variability did not increase with time. Indeed, their measure of response similarity was equivalent within and across days. In what now reads as a prescient anticipation of the drift phenomenon, Bhalla and Bower concluded: "it is clear, at least over five days, that the cell is bounded in how it can respond. If this were not the case, we would expect a continual increase in relative response variability over multiple days (the equivalent of response drift). Instead, the degree of variability in the responses of single cells is stable over the length of time we have recorded." Thus, even at the level of single cells, this early paper argues that the bulb is stable.

This basic result has since been replicated by several groups. Kato et al. (2012) used chronic two-photon calcium imaging of mitral cells in awake, head-fixed mice and likewise found that, while odor responses could be modulated by recent experience (odor exposure leading to transient adaptation), the underlying tuning of individual cells remained stable. While experience altered mitral cell odor responses, those responses recovered to their original form at the level of the single neuron, maintaining tuning over extended periods (two months). More recently, the Mizrahi lab (Shani-Narkiss et al., 2023) extended chronic imaging to six months, reporting that single-cell odor tuning curves remained highly similar over this period. These studies reinforce Bhalla and Bower's original conclusion: despite trial-to-trial variability, olfactory bulb neurons maintain stable odor tuning across extended timescales, with plasticity emerging primarily in response to experience. (The Yamada et al., 2017 paper, which the authors here cite, is not an appropriate comparison. In Yamada, mice were exposed daily to odor. Therefore, the changes observed in Yamada are a function of odor experience, not of time alone. Yamada does not include data in which the tuning of bulb neurons is measured in the absence of intervening experience.)

Therefore, a model that relies on instability in the tuning of bulbar neurons risks giving the incorrect impression that the bulb drifts over time. This difference should be explicitly addressed by the authors to avoid any potential confusion. Perhaps the best course of action would be to fit their model to Mizrahi's data, should this data be available, and see if, when constrained by empirical observation, the model still produces drift in piriform. If so, this would dramatically strengthen the paper. If this is not feasible, then I suggest being very explicit about this difference between the behavior of the model and what has been shown empirically. I appreciate that in the data there is modest drift (e.g., Shani-Narkiss' Figure 8C), but the changes reported there really are modest compared to what is exhibited by the model. A compromise would be to simply apply these metrics to the model and match the model's similarity to the Shani-Narkiss data. Then the authors could ask what effect this has on drift in piriform.

The risk here is that people will conclude from this paper that drift in piriform may simply be inherited from instability in the bulb. This view is inconsistent with what has been documented empirically, and so great care is warranted to avoid conveying that impression to the community.

We thank the reviewer for highlighting this important issue. We agree that the interpretation of our model requires care to avoid implying that the olfactory bulb exhibits spontaneous drift. As the reviewer points out, the empirical literature shows that M/T-cell tuning is highly stable for infrequently experienced odors, but can change with daily, persistent odor exposure (e.g., Kato et al., 2012; Yamada et al., 2017).

We thank the reviewer for highlighting the Bhalla and Bower paper, as it is foundational and actually raises a number of interesting and important points. As the authors noted, there was significant variability in trial-to-trial responses over sessions and days in single neurons. This is likely due to on-going dynamics (Laurent, 1999), the impact of behaviorally relevant top-down feedback (Chen and Padmanabhan, 2022), decision making (Kay and Laurent, 1999), and an array of factors that our model does not include. In that manuscript, the authors note “the variability of the same neuron recorded over different days…was not statistically different from the within day comparisons.” While these results appear prima facie to be different from our results, there are several reasons why they may not be the case.

First, different metrics are used for measuring neuronal stability, which may contribute to some of the differences. Second, and perhaps more importantly and interestingly, the authors in that study noted the significant trial-to-trial variability within day, which is not present in our study because our model has none of the richness of behavior that Bhalla and Bower found in the freely behaving rat. This variability within day (which is much higher than what we report) would reduce the impact of drift across days - a result that would complicate how plasticity across multiple timescales occurs. We thank the reviewer for the insights on this critical study and include these points in our discussion (line 321-330).

Neural responses to odor representations are incredibly variable across different time scales (Padmanabhan and Urban 2010, Angelo et al 2011, Kapoor and Urban 2006, Friedrich and Laurent, 2001, Smear et al 2011, Wesson et al 2008). In our model, none of this selection of survival related to behavior is included, nor are there specific rules about which synapses may be preferentially strengthened (due to neuro modulation corresponding to behavioral choice and reinforcement learning). Instead, we aimed to recapitulate the experimental design of a few studies (Kato et al 2012, Yamada et al, 2017) to understand how neurogenesis and drift are related. Over the simulated 10 days, the odor is presented every day, and the network is otherwise frozen between sessions—meaning the model lacks mechanisms that would normally support recovery during intervals without odor exposure. Under these conditions, adult neurogenesis effectively interacts with repeated experience, producing gradual changes in individual M/T-cell tuning. Thus, our results should be interpreted as modeling experience dependent changes over the timescale of neurogenesis, not as evidence for spontaneous drift in the bulb. We now state this explicitly in the Discussion to prevent confusion and expand the discussion to incorporate some of these critical ideas (line 321-330).

Major comments (all related to the above point)

(1) Lines 146-168: The authors find in their model that "individual M/T cells changed their responses to the same odor across days due to adult-neurogenesis, with some cells decreasing the firing rate responses (Fig.2A1 top) while other cells increased the magnitude of their responses (Fig. 2A2 bottom, Fig. S2)" they also report a significant decrease in the "full ensemble correlation" in their model over time. They claim that these changes in individual cell tuning are "similar to what has been observed by others using calcium imaging of M/T cell activity (Kato et al., 2012 and Yamada et al., 2017)" and that the decrease in full ensemble correlation is "consistent with experimental observations (Yamada et al., 2017)." However, the conditions of the Kato and Yamada experiments that demonstrate response change are not comparable here, as odors were presented daily to the animals in these experiments. Therefore, the changes in odor tuning found in the Kato and Yamada papers (Kato Figure 4D; Yamada Figure 3E) are a function of accumulated experience with odor. This distinction is crucial because experience-induced changes reflect an underlying learning process, whereas changes that simply accumulate over time are more consistent with drift. The conditions of their model are more similar to those employed in other experiments described in Kato et al. 2012 (Figure 6C) as well as Shani-Narkiss et al. (2023), in which bulb tuning is measured not as a function of intervening experience, but rather as a function of time (Kato's "recovery" experiment). What is found in Kato is that even across two months, the tuning of individual mitral cells is stable. What alters tuning is experience with odor, the core finding of both the Kato et al., 2012 paper and also Yamada et al., 2017. It is crucial that this is clarified in the text.

We thank the reviewer. As the issue raised here is related to the previous comment, we have clarified this in the revised text to avoid any misleading comparison and specify what aspects of our computational model map onto experimental studies and what aspects we cannot recapitulate and as a result, the places where our comparisons are limited.

(2) The authors show that in a reduced-space correlation metric, the correlation of lowdimensional trajectories "remained high across all days"..."consistent with a recent experimental study" (Shani-Narkiss et al., 2023). It is true that in the Shani-Narkiss paper, a consistent low-dimensional response is found across days (t-SNE analysis in Shani-Narkiss Figure 7B). However, the key difference between the Shani-Narkiss data and the results reported here is that Shani-Narkiss also observed relative stability in the native space (Shani-Narkiss Figure 8). They conclude that they "find a relatively stable response of single neurons to odors in either awake or anesthetized states and a relatively stable representation of odors by the MC population as a whole (Figures 6-8; Bhalla and Bower, 1997)." This should be better clarified in the text.

We agree with the reviewer that some of the cells in Shani-Narkiss Figure 8B showed relatively stable responses (while others did not). However, there is a clear monotonic increase in the “Average differences” over time, from “Same day” to “1 month” to “6 month”, as quantified in their Figure 8B. Although the author concluded that they "find a relatively stable response of single neurons”, we would argue that their data also provided evidence for what we would term “relatively unstable responses” as found in our model. But per reviewer’s suggestion, we better clarify it in the text now (line 194197).

(3) In the discussion, the authors state that "In the MOB, individual M/T cells exhibited variable odor responses akin to gain control, altering their firing rate magnitudes over time. This is consistent with earlier experimental studies using calcium-imaging." (L3146). Again, I disagree that these data are consistent with what has been published thus far. Changes in gain would have resulted in increased variability across days in the Bhalla data. Moreover, changes in gain would be captured by Kato's change index ("To quantify the changes in mitral cell responses, we calculated the change index (CI) for each responsive mitral cell-odor pair on each trial (trial X) of a given day as (response on trial X - the initial response on day 1)/(response on trial X + the initial response on day 1). Thus, CI ranges from −1 to 1, where a value of −1 represents a complete loss of response, 1 represents the emergence of a new response, and 0 represents no change." Kato et al.). This index will capture changes in gain. However, as shown in Figure 4D (red traces), Figure 6C (Recovery and Odor set B during odor set A experience and vice versa), the change index is either zero or near zero. If the authors wish to claim that their model is consistent with these data, they should also compute Kato's change index for M/T odor-cell pairs in their model and show that it also remains at 0 over time, absent experience.

We appreciate the reviewer’s suggestion and edited the text to make it more accurate (line 319-320).

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) Line 28 "a graduate alteration in sensory perception". We do not know if drift results in changes in perception. If anything, behavioral evidence suggests that perception remains stable in spite of drift. For example, in Driscoll et al. (2017) mice are able to successfully navigate a virtual T maze despite drift, and in Schoonover et al. (2021), mice maintain aversive responses following fear conditioning, despite drift in the piriform. Finally, spatial navigation appears unimpaired despite pronounced drift in the hippocampus (e.g., Climer et al., 2025). It would be more appropriate to say "stimulusevoked activity patterns" than "sensory perception" or other words that refer to neuronal activity rather than cognition or behavior.

We edited the text to make it more accurate per the reviewer’s suggestion (line 27).

(2) In the introduction, the authors state: "This representational drift has led to the hypothesis that PCx, rather than being a primary sensory area, may be more like an association cortical region." (L76-78). However, the hypothesis that PCx operates as an association cortex comes originally from Haberly's work and thinking (e.g., Haberly and Bower, 1984, elaborated in extensive detail in Haberly, 2001). I think it would be appropriate to acknowledge that here.

We added the references to make acknowledge that per the reviewer’s suggestion (line 77).

(3) In the methods, the authors elegantly describe how they induce neurogenesis in their model using weight reshuffling (L805-814). I think it could really help the reader understand the model if this idea were also included in the results section. As the results section currently reads, it seems as if their model implemented neurogenesis in a different fashion: "To do this, following elimination of 10% of the GCs in the network, we added new cells and randomly assigned synaptic weights between these abGCs and M/Ts". I appreciate that in their model, shuffling all the weights of a given GC randomly is akin to "elimination", but I feel like at first blush the results section risks giving an impression a bit different than that actually used in the model.

We edited the text to make it more accurate per the reviewer’s suggestion (line 110-112).

eLife Assessment

This manuscript introduces a new low-cost and accessible method for assembling combinatorially complete microbial consortia using basic laboratory equipment, which is a valuable contribution to the field of microbial ecology and biotechnology. The evidence presented is compelling, demonstrating the method's effectiveness through empirical testing on both synthetic colorants and Pseudomonas aeruginosa strains.

Reviewer #1 (Public review):

This work develops a simple, rapid, low-cost methodology for assembling combinatorially complete microbial consortia using basic laboratory equipment. The motivation behind this work is to make the study of microbial community interactions more accessible to laboratories that lack specialized equipment such as robotic liquid handlers or microfluidic devices. The method was tested on a library of Pseudomonas aeruginosa strains to demonstrate its practicality and effectiveness. It provided a means to explore the complex functional interactions within microbial communities and identify optimal consortia for specific functions, such as biomass production.

The primary strength of this manuscript lies in its accessibility and practicality. The method proposed by the authors allows any laboratory with standard equipment, such as multichannel pipettes and 96-well plates, to readily construct all possible combinations of microbial consortia from a given set of species. This greatly enhances access to full factorial designs, which were previously limited to labs with advanced technology.

Another strength of the manuscript is the measurement and analysis of the biomass of all possible combinations of 8 strains of P. aeruginosa. This analysis provides a concrete example of how the authors' new methodology can be used to identify the best-performing communities and map pairwise and higher-order functional interactions.

Notably, the authors do exceptionally well in providing a thorough description of the methodology, including detailed protocols and an R script for customizing the method to different experimental needs. This enhances the reproducibility and adaptability of the methodology, making it a valuable resource for researchers wishing to adopt this methodology.

Comments on revisions:

I thank the authors for their response. The revisions have addressed all of the issues raised in my original review, and I believe they have improved the clarity of the manuscript.

Reviewer #3 (Public review):

The author developed a useful methodology for generating all combinations of multiple reagents using standard lab equipment. This methodology has clear uses in for studying of microbial ecology as they demonstrated. The methodology will likely be useful for other types of experiments that required exhaustive testing of all possible combinations of a given set of reagents (e.g., drug-drug antagonism and synergy).

The authors provided a useful R script that generates a detailed experimental protocol for building desired combination from any number of reagents. The produced document is useful and has clear instructions. The output of the computer script will be strengthened if graphical output is also provided (similar to the one provided in Figure 1C).

The authors show that the error rate of the method doesn't go up with the number of combinations using dyes (Figure 2).

The authors demonstrate the value of their methodology for studying interactions within microbial consortia by assembling all possible combinations of eight strains of Pseudomonas aeruginosa. The value of their methodology for this application is well founded. However, it is also unclear why specific experimental choices were made for this application. It is unclear why authors continue to show the absorbance measurements of strain assemblies over the entire wavelength spectrum and not just for ABS 600 nm (figures 3 and 4). It is also unclear why the authors provided information on the "sum of the three spectra" as this reference line is meaningless and not a reasonable null model for estimating how well specific strain combinations will grow together.

Figure 5 illustrates the various analysis types that can be performed on the data collected from growing combinations of eight Pseudomonas aeruginosa strains. It is a very informative figure since it provides a "roadmap" on the various ways in which the dataset produced can be explored. The information in Figure 5 and S6 will likely be very useful for a wide audience.

Comments on revisions:

We thank the author for considering the review and providing additional clarifications. The authors disagree with some of the points we raised and decided to reject some of our recommendations. All the points of disagreement are minor and clearly subjective (e.g., stylistic). Congratulations again for this elegant manuscript.

Author response:

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

Reviewer #1 (Public review):

This work develops a simple, rapid, low-cost methodology for assembling combinatorially complete microbial consortia using basic laboratory equipment. The motivation behind this work is to make the study of microbial community interactions more accessible to laboratories that lack specialized equipment such as robotic liquid handlers or microfluidic devices. The method was tested on a library of Pseudomonas aeruginosa strains to demonstrate its practicality and effectiveness. It provided a means to explore the complex functional interactions within microbial communities and identify optimal consortia for specific functions, such as biomass production.

The primary strength of this manuscript lies in its accessibility and practicality. The method proposed by the authors allows any laboratory with standard equipment, such as multichannel pipettes and 96-well plates, to readily construct all possible combinations of microbial consortia from a given set of species. This greatly enhances access to full factorial designs, which were previously limited to labs with advanced technology.

Another strength of the manuscript is the measurement and analysis of the biomass of all possible combinations of 8 strains of P. aeruginosa. This analysis provides a concrete example of how the authors' new methodology can be used to identify the best-performing communities and map pairwise and higher-order functional interactions.

Notably, the authors do exceptionally well in providing a thorough description of the methodology, including detailed protocols and an R script for customizing the method to different experimental needs. This enhances the reproducibility and adaptability of the methodology, making it a valuable resource for researchers wishing to adopt this methodology.

We thank the reviewer for their thoughtful comments and positive assessment of our work. Below we detail the changes we have introduced in the manuscript to clarify issues raised by the reviewer.

While the methodology is robust and well-presented, there are some limitations that should be acknowledged more thoroughly. First, the method's scalability is an important factor. The authors indicate that it should be effective for up to 10-12 species, but there is no discussion of what sets this scale: time, amount of labor, consumables, the likelihood of error, sample volume, etc.

The 10-12 species estimation is based on our own experience implementing the protocol, and set primarily by time, labor, and consumables (as rightly pointed out by the reviewer) rather than conceptual limitations of the approach. We have added clarifications in the Discussion (lines 401-405) regarding these scalability-limiting factors.

Second, this methodology is tailored to construct communities where the abundance of each strain is identical in each combination. Therefore, combinations with a different number of strains also differ in the total initial amount of microbial cells. Second, variations in the initial proportions of the same set of strains cannot be readily explored.

Note that the “density homogenization” step is optional and it could be skipped entirely, which would result in a same species being present at variable densities across consortia: specifically, skipping this step would make the density of a species in a consortium inversely proportional to the number of species in that consortium. Further variations in initial abundance could be explored by treating a same strain at two (or more) starting abundances as distinct inputs of the protocol – though this would naturally increase the number of combinations to test.

We have included a paragraph in the Discussion (lines 416-423) describing how we can, in principle, extend our protocol to explore abundance effects.

Third, the manuscript only discusses how to construct the combinations, and not how to assay them afterward (e.g. for community function, interspecific interactions, etc.). While details on how to achieve these goals are clearly outside the scope of this work, the use of biomass as an example function may obfuscate this caveat, which should be stated more explicitly.

We agree that the manuscript focuses exclusively on the construction of microbial communities and does not address how these communities should be assayed afterward. This is an intentional scope decision. The proposed protocol is fully compatible with a wide range of functional, interaction-based, or omics-based assays. Absorbance is mentioned as an illustrative example of a possible readout, rather than as a recommended or exclusive parameter. We have revised the text to explicitly state that the assessment of community function or interspecific interactions lies outside the scope of this work and must be tailored to the specific biological question being addressed.

Reviewer #1 (Recommendations for the authors):

A few specific technical notes and notes about clarity:

(1) It may be worth being more explicit about how to produce replicates. For example, producing technical replicates by inoculating multiple times from the same set of combinations, while biological replicates require making the combinations multiple times.

We have updated the main text to clarify this point (line 780-781).

(2) Figure 2C: May be worth adding some context to these performance numbers. What are typical accuracies? What would they be in a liquid handler?

Assessing typical accuracies is nuanced since the error depends not only on the assembly steps, but also on potential intrinsic variation of the specific community function being tested and the method used to quantify it. One of the main reasons for including the experiment using colorant combinations was precisely to minimize these other sources of variation. In this experiment, we find that the error we quantify is consistent with cumulative pipetting variation (as a reference, a typical lab micropipette has an error of 0.5-1%). This is now explicitly mentioned in the manuscript.

(3) Figure 5A: I realize it is unlikely that strains go extinct in these experiments. But it is still worth clarifying that the number of strains is the number inoculated, rather than the one present at the time of measurement.

We updated the caption of Figure 5A as recommended by the reviewer.

(4) Figure 5B: I realize this is just for illustration purposes, but you should provide more information about the magnitude of the difference in performance of these combinations and the confidence in their ranking (or variability in performance across replicates).

Following this suggestion, we have added a paragraph where we report the variation across replicates for the highest-performing consortia (lines 318-323). Indeed, while variation across replicates is small, it is enough to produce an overlap between the confidence intervals of the function of some of the highest-performing consortia. This is now explicitly acknowledged in the manuscript.

(5) Figure 5C: I believe the bold black lines indicate the combinations shown in panel D, but that is not explicitly stated.

We have updated the caption of Figure 5C.

Reviewer #2 (Public review):

A simple and effective method for combinatorial assembly of microbes in synthetic communities of <12 species.

Overall, this manuscript is a useful contribution. The efficiency of the method and clarity of the presentation is a strength. It is well-written and easy to follow. The figures are great, the pedagogical narrative is crisp. I can imagine the method being used in lots of other contexts too.

The authors could better clarify what HOIs mean. They could address challenges with assaying community function. However, neither of these “weaknesses” affects the primary goal of the paper which is methodological.

We thank the reviewer for the positive assessment. With respect to HOIs, we recognize that defining and quantifying them is a non-trivial subject within the broader field of microbial ecology (see e.g. ref. 24 within the manuscript). Since our aim with this manuscript is methodological, as the reviewer notes, here we have done our best to avoid introducing new or ambiguous definitions. For this reason, we simply adopt a definition given in previous works (including refs. 10, 19, 24, 29, 37, and 38 in the manuscript), where the context-dependence of pairwise interaction terms is taken as a signature of HOIs. With respect to the challenges in assaying community function, please see our responses below.

Reviewer #2 (Recommendations for the authors):

Overall, this manuscript is a useful contribution, I appreciate the authors taking the time to write it up! I have a few relatively minor comments.

(1) It would be nice in the introduction to address why we might want the full factorial construction of communities in the first place. This is an especially relevant question in light of the authors' 2023 Nat E&E paper where they showed that the function of communities can often be learned even when only a fraction of all possible communities is measured. This is addressed in part in the paragraph on line 34, but I think it might be worth expanding a bit given the focus on the paper.

We sincerely appreciate the reviewer’s feedback. In fact, one of the reasons that make full factorial construction desirable is precisely to test theoretical and computational models of community function, including (but not only) the statistical models developed in our 2023 Nature E&E paper. In that work, we showed that low-order models can explain a substantial fraction of the variation in community function in previously-published datasets, but we also predict that the same models could fail under complex structures of microbial interactions (e.g., strong high-order interactions). The protocol we present here enables the empirical quantification of such interactions, making this prediction (and others) directly testable. We have included that clarification in the revised manuscript (lines 56-58).

(2) Around line 74, I think it is worth mentioning that even this elegant design will face insurmountable practical challenges (time, liquid handling operations, number of plates will explode) for full factorial design with 20, 30, 40 species or more. This is relevant for some very complex synthetic consortia that some microbiome groups are constructing (e.g. hCom2 from Huang/Fishbach groups) https://www.sciencedirect.com/science/article/pii/S0092867422009904.

We agree with the reviewer that full factorial designs become impractical for very large species pools. These limits are now more clearly mentioned in the revised manuscript. We refer the reviewer to our response to comment #1 by Reviewer 1 for further details.

(3) The binary construction is a really nice clean way to explain the protocol. Appreciate the pedagogy!

We thank the reviewer for the appreciation.

(4) In the experiment with pseudomonas strains the consortia are grown in LB. This medium will support growth to relatively high OD (>1). At these densities, the change in OD with density is almost certainly not linear with cell density, and this nonlinearity likely depends on strain identity. In this case, the assumption of additivity may not hold. As a result, some of the observed "interactions" may simply be non-linearity in the assay and not the abundance of bacteria in the communities. Of course, this does not affect the assembly protocol in any way, but it does complicate the interpretation of interactions via this assay. I think this is worth pointing out since other researchers may have to think carefully about the assay they use when constructing these synthetic consortia. I think in this methods paper it is important to emphasize this so other researchers do not mistakenly identify interactions due to issues with the assay.

We thank the reviewer for pointing out this important aspect. In our experiment, we use Abs₆₀₀ simply as an example of a measurable community-level function. The reviewer is absolutely correct in that mapping absorbance to biomass is nuanced at large OD values, where this relationship becomes non-linear. While this is not an issue from the perspective of the protocol itself, it is indeed an important consideration for users who may want to obtain reliable quantifications of biomass. We have updated the manuscript to explicitly mention this potential issue (lines 307-313). We have also emphasized the fact that our focus on Abs₆₀₀ is strictly for illustrative purposes, and we have removed all instances where a direct mapping from Abs₆₀₀ to biomass was implied in the text.

(5) Subtle point regarding HOIs. HOI (or pairwise) statistical interactions need not quantitatively be the same as interactions in a lotka volterra sense. I realize the authors do not explicitly use the term "interaction" in an gLV model formalism but this is how the majority of readers will interpret this term. I believe it is a research question as to how pairwise gLV interactions manifest themselves in terms of functional interactions. For example, a purely pairwise LV model could easily have HOI "functional interactions" if the function is total abundance since abundances depend nonlinearly on LV interactions. I think this part of the manuscript could be confusing to readers for this reason. I think the term "functional interaction" really helps with this issue, but just asking the authors to make sure this is clear.

I say this because ref: 37 is focused on HOIs in an LV sense. Here, as the authors are aware, they are computing statistical "interactions" in the sense of epistasis. Given that they are computing this epistasis averaged across all community compositions a more appropriate citation might be [https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1004771] where the same quantity is computed in a protein context.

We thank the reviewer for pointing out this important issue. Indeed, we use the term “interaction” in a statistical sense (as the deviation of the observed community function from a null, additive expectation) rather than in a Lotka-Volterra sense. We agree that the reference suggested by the reviewer is more appropriate in this context. We have updated the reference list accordingly.

(6) Figure 5G - a little hard to see. Any way to show this data more clearly? It looks like all interactions have a mean of 0 because of the way the data are presented.

The reviewer is indeed correct in that, as defined, the interactions that we quantify are back ground dependent, and their average across backgrounds lies near zero for all species. More than an issue with the representation, we think that this is an important empirical observation: it indicates that a same species pair may interact positively or negatively depending on its ecological context. We believe that the current representation is most appropriate for making this clear, but we would be open to discussing alternatives if the reviewer had a specific suggestion in mind.

Reviewer #3 (Public review):

The authors developed a useful methodology for generating all combinations of multiple reagents using standard lab equipment. This methodology has clear uses for studying microbial ecology as they demonstrated. The methodology will likely be useful for other types of experiments that require exhaustive testing of all possible combinations of a given set of reagents (e.g., drug-drug antagonism and synergy).

The authors provided a useful R script that generates a detailed experimental protocol for building the desired combination from any number of reagents. The produced document is useful and has clear instructions. The output of the computer script will be strengthened if graphical output is also provided (similar to the one provided in Figure 1C).

The authors show that the error rate of the method doesn't go up with the number of combinations using dyes (Figure 2).

The authors demonstrate the value of their methodology for studying interactions within microbial consortia by assembling all possible combinations of eight strains of Pseudomonas aeruginosa. The value of their methodology for this application is well-founded. However, it is also unclear why specific experimental choices were made for this application. It is unclear why authors continue to show the absorbance measurements of strain assemblies over the entire wavelength spectrum and not just for ABS 600 nm (Figures 3 and 4). It is also unclear why the authors provided information on the "sum of the three spectra" as this reference line is meaningless and not a reasonable null model for estimating how well specific strain combinations will grow together.

Figure 5 illustrates the various analysis types that can be performed on the data collected from growing combinations of eight Pseudomonas aeruginosa strains. It is a very informative figure since it provides a "roadmap" on the various ways in which the dataset produced can be explored. The information in Figures 5 and S6 will likely be very useful for a wide audience.

Reviewer #3 (Recommendations for the authors):

(1) Congratulations. I think the manuscript lays out a simple and very elegant methodology that will be useful for many. While I think the method is overall well explained and rationalized, the paper can greatly benefit from further expansion of Figure 5 at the expense of Figures 3 and 4.

We thank the reviewer for their thoughtful assessment of our work. We have considered the recommendations and discuss the following points in response.

(2) Unless I am missing something, there is no reason to present data collected across the entire wavelength spectrum for microbial assemblies (Figures 3 and 4). Moreover, using the same color palette for bacterial strains (Figure 3A) and colorants (Figure 2) is highly confusing. I suggest considering using only the 600 nm wavelength for any data collected from microbial assemblies and using a very different color palette for bacteria and colorants to avoid misinterpretation of the data.

We thank the reviewer for this suggestion. Our goal with Figures 3-4 was to illustrate the convenience of the protocol and the ease with which many measurements can be performed in parallel once the combinatorial assembly has been completed. While we focus on Abs₆₀₀ for all subsequent analyses, we chose to display the full spectra in Figs. 3-4 in hopes that future studies can make use of our rich dataset to interrogate questions on microbial interactions, with the option to focus on other wavelengths (which can effectively be treated as different community-level functions in their own right; for instance, we have previously used Abs₄₀₅ as a proxy for siderophore concentration). We think there is value in Figs. 3-4 in their current form to make this clear to readers.

(3) Unlike dye absorbance, bacterial carrying capacity has an upper limit, so summing individual population absorbance as a reference line seems unjustified. If the summation of absorbance is meant to provide a "null model" for expected growth, a more suitable model should be considered (e.g., max spectra or a weighted sum of the spectra from individual members).

We agree with the reviewer that our null model is not biologically constrained, and we did not intend to imply that the additive expectation was derived from biological principles. Instead, this additive expectation should be interpreted as a simple statistical baseline with minimal assumptions. The use of an additive baseline for quantifying microbial interactions has been addressed in the literature (see, e.g., references 10, 19, 24, 29, 37, and 38), and so here we chose to conform to this convention to avoid introducing new, non-standard quantifications of pairwise and higher-order interactions. We have revised the text to make this more explicit.

(4) The R script is a valuable tool. I think that a valuable improvement will be to also generate visual representations as part of the script’s output such as the colored plates in Figure 1C that are specific to the generated protocol.

We have updated the script so that it now also outputs a table specifying the location of each consortium within the plates. We chose to make this a text, rather than a graphics output, to ensure cross-device compatibility.

(5) The discussion rightly acknowledges the potential to extend the protocol to larger libraries using liquid handlers. To facilitate this implementation, it might be beneficial to modify the script output so that the ‘volume’, ‘plate’, and ‘column’ values are tab- or comma-delimited.

We thank the reviewer for the suggestion. We have modified the output so that it is now tab-delimited.

(6) Figures 3 and 4 do not provide a lot of insight. I would suggest combining them into a single figure and using only absorbance values at 600 nm. It would also be interesting to add a histogram of these absorbance values and possibly show histograms for subgroups (e.g. all assemblies with more than 3 strains vs all assemblies with 3 or fewer strains).

With respect to Figs. 3 and 4, we refer the reviewer to our response to comment #2. With respect to the histogram/subgroups plot, we understand that this would be a slightly modified version of the current Fig. 5A, where we show means and standard deviations across all subgroups of 1 to 8 species, and so we find it unclear what this figure would add.

(7) With the recommendations of removing or reworking Figures 3 and 4, and the fact that Figure 5 is data-rich (and extremely useful), it would be beneficial to split Figure 5 and include the data shown in Figure S6 in the main figure. The analysis in Figure 6S is valuable and it might be beneficial to elevate this analysis to a primary figure and provide a detailed explanation of its rationale and methods in the main text.

We appreciate this suggestion. In our view, we find that both the text and the figures benefit from a heavy focus on the assembly protocol, as this is the main contribution of this work. While we do think it is valuable to highlight the type and amount of data that can be collected with a full factorial assembly, as well as the types of analyses that can be performed with this data, we are afraid that allocating more space to these analyses may distract readers from the methodology itself. We have therefore chosen to keep the original structure for Figs. 5 and S6.

eLife Assessment

This study presents valuable findings by reanalyzing previously published MEG and ECoG datasets to challenge the predictive nature of pre-onset neural encoding effects. The evidence supporting the central conclusions remains incomplete, as additional details of the analyses are needed and alternative interpretations, such as the possibility that pre-onset predictive and sensory-evoked responses rely on distinct neural representations, have not been sufficiently addressed. The work may be of interest to researchers in language processing, predictive coding, and related fields.

Reviewer #1 (Public review):

The manuscript analyzes previously published MEG and ECoG datasets to examine pre-onset neural encoding effects during language processing, replicating effects that have been reported in earlier work and demonstrating that they persist even after controlling for correlations in the stimulus sequence. Replication of these effects across recording modalities and datasets is a valuable contribution, as it strengthens confidence in the robustness of anticipatory neural activity related to upcoming linguistic input. However, I have significant concerns regarding the interpretation of these findings, particularly the conclusion that the absence of temporal generalization between pre- and post-onset activity implies that pre-onset activity does not reflect predictive pre-activation of the upcoming word.

The central inferential step in this argument relies on an implicit assumption: that if the brain were predicting an upcoming word, the neural representation prior to word onset should resemble, or generalize to, the representation observed after word onset. This assumption is not theoretically necessary and is not supported by a substantial body of work on predictive processing. Many contemporary models posit that predictions are represented in abstract, compressed, or probabilistic formats that differ from sensory-evoked representations, particularly in hierarchical systems such as language (e.g., Rao & Ballard, 1999; Friston, 2005; Federmeier, 2007; Kuperberg & Jaeger, 2016; de Lange et al., 2018). Under such accounts, predictive representations may encode expectations over latent semantic features or probability distributions rather than reinstating the neural code associated with perceptual input.

In this context, the temporal generalization analyses presented here convincingly demonstrate that pre-onset and post-onset activity do not share a stable representational code. However, this result does not rule out predictive processing per se. Rather, it rules out a specific and relatively strong hypothesis: that prediction takes the form of early reinstatement of the same neural representation used during post-onset word processing. The data are equally consistent with the interpretation that pre-onset activity reflects predictive information expressed in a different representational format that is transformed upon stimulus onset.

I therefore recommend that the authors substantially soften and clarify their conclusions regarding prediction. Statements suggesting that pre-onset activity does not reflect prediction should be revised to more precisely reflect what is directly supported by the analyses, namely, the absence of representational identity or stable overlap between pre- and post-onset activity. Explicit acknowledgement of alternative interpretations grounded in established predictive processing frameworks would improve theoretical alignment and avoid overstating the implications of the temporal generalization results.

Overall, the empirical analyses are carefully executed, and the replication across datasets is a strength. However, the current framing risks over-interpreting what the data can rule out about prediction. A clearer distinction between representational equivalence and predictive processing would significantly strengthen the manuscript's theoretical contribution.

Reviewer #2 (Public review):

Summary:

The authors show that pre-onset neural encoding is likely not a product of predictive processing. They demonstrate this primarily through two analyses:

(1) They decorrelate the neural responses between pre- and post-word onset and show that this does not eliminate pre-onset neural encoding. This suggests that this pre-onset neural encoding is not a result of pre-activation driven by an underlying predictive process.

(2) They show that the future word improvement to encoding performance shown in Caucheteux et al. is likely a result deriving from the low temporal resolution in fMRI, as it does not reproduce in MEG or ECoG data, modalities that have a higher temporal resolution better suited to this kind of analysis.

Strengths:

Both of the paper's arguments are overall very compelling and point to potential problems in the underlying literature that may require reevaluation. The paper does not make any unreasonable claims. The limitations of the study are appropriately addressed. The paper is well-reasoned and well-written. Overall, I believe the paper is a worthy addition to the literature on this subject.

Weaknesses:

One concern is that I wonder about the degree to which the residualization/decorrelation that the authors employ in Figure 4 is truly forcing the model to unlearn all the interactions between pre- and post-word onset when referencing the neural activity. This point is explicitly noted in Schonmann et al. (which the authors cite): "While residualised word embeddings no longer contain temporal stimulus dependencies, these dependencies are still represented in the neural data, and can hence be 're-learned' when fitting the regression model." I imagine the inverse of this could be true here - the dependencies are still represented in the stimulus and so can be relearned when mapping to the neural data. It is possible that the small positive onset correlation that occurs after decorrelation can be entirely explained by this. This is not a bad thing per se (as it aligns with the overall point of the article), but it is a potential methodological oversight. A clear description of the decorrelation process is necessary in the methods section.

The paper correctly notes that their removal of bigram/n-gram information does not entirely exclude all stimulus dependencies. However, removing this fully would be extremely difficult, and the small reduction in performance of the bigram-ablated model does not point to this being a major issue.

Separately, some of the figures are a little rough. Suggestions have been provided to the authors.

Reviewer #3 (Public review):

Previous studies have shown that language model embeddings of future words can predict brain responses to language. This has been interpreted as evidence for predictive representations in the brain. The primary finding of the present study is that this index of predictive processing is not consistent with a pre-activation account, but instead suggests continuously evolving representations. A strength of the manuscript is that it uses methods that build on previous studies and shows that previous results replicate in the current datasets, before testing new hypotheses. Addressing some minor weaknesses would further strengthen the results and ascertains that the conclusions are justified:

(1) When analyzing neural data, "words with multiple tokens assigned by the model were excluded" (11). I am wondering whether this could have had an influence on the results. I suspect that using only single token words would bias the dataset towards semantically light high frequency and function words. Pre-activation may be different for those words from more semantically rich, longer words.

(2) The study only used a context window of 50 tokens for language model predictions (11). This is less than in previous studies, and may constitute a confound when comparing results across studies. This may be particularly relevant in comparison to Caucheteux et al. (2003), whose results suggested more extensive predictions (9), which may require more extensive context.

(3) The manuscript is largely missing data on the reliability of the results. Some form of significance test, and indication of variability and/or the noise floor in the figures would be helpful.

A primary concern when analyzing naturalistic speech data is that different speech features are highly correlated across linguistic levels and across time. The manuscript makes a reasonable effort to control for stimulus autocorrelations. It is encouraging that the effect survived this correction. As the manuscript concedes, control is not perfect and controlling for "all regularities inherent to natural speech" remains a challenge (9). This should be kept in mind when interpreting the results.

Finally, the manuscript also argues that "we observed clear signatures of postdiction, with neural activity reflecting persistent encoding of prior words" (abstract). I did not follow this reasoning. The ostensible evidence for this is that "including the previous word ... improves encoding even after the current word's onset" (Figure 5). However, this is not further surprising, because the previous word can often only be recognized around the end of the word, corresponding to the time of the current word onset. Language model embeddings reflect a contextual semantic interpretation of the word, which likely requires further processing after word recognition. I would thus expect that the initial contextual interpretation of a word occurs during presentation of the subsequent word. Evidence for "persistent encoding" should include encoding beyond this point, i.e., over the course of several subsequent words. Contrary to this, Figure 5 a (left) suggests that the predictive effect of the previous word (d-1) stops around the offset of the current word (d). This suggests to me that, once controlling for subsequent embeddings, the embedding of a word disappears from the neural activity soon after word recognition.

Author response:

Reviewer 1:

We thank the reviewer for bringing a critical theoretical distinction to our attention. We agree that the Temporal Generalization (TG) results specifically rule out the reinstatement of post-onset neural codes, the idea that the brain pre-activates the same neural representation evoked by the stimulus. In fact, we mention in the discussion: "This temporal variability underscores the need for a more nuanced view of what constitutes predictive pre-activation, as no stable representational state appears to persist after word presentation that could serve as its target.".

To our understanding, prediction is rarely explicitly defined in the literature, and the distinction between predictive pre-activation and other forms of prediction is seldom made. Moreover, the idea of compressed or abstract forms of pre-activated representations has not, to our knowledge, been explicitly articulated in the literature. Our TG findings therefore, put meaningful constraints on theories of prediction. In the revisions we will expand on this more and include a broader description of potential forms of pre-activation. We will emphasize that the TG results specifically rule out that the brain pre-activates the same neural code used for sensory-evoked processing.

Moreover, although TG analysis does not rule out alternative notions of predictive pre-activation, we believe our second analysis (the inclusion of future word embeddings) provides independent evidence that argues against more abstract forms of prediction. Unlike the TG analysis, this encoding approach is not constrained to a specific neural code; if the brain represented upcoming words in any linearizable format (abstract, probabilistic, or latent) incorporating those embeddings should have improved the brain score at the current word's onset. We found no such improvement until the word was actually heard. In the revised manuscript, we will reformulate the narrative to clarify that while TG alone rejects a specific form of pre-activation, the combined evidence from both analyses suggests there is a broader lack of predictive pre-activation.

Reviewer 2:

We thank the reviewer for their constructive feedback and for bringing to our attention the missing information in our Methods section. We realized that the final two sections were inadvertently omitted during formatting changes before submission. These will be restored in the revised version.

We appreciate the reviewer's careful reading of this analysis and agree that the concern whether the decorrelation in figure 4 forces the model to unlearn the associations between pre- and post-onset activity is a valid one. To clarify, this is not what we intended to claim. Rather, our argument follows a different logic: if we assume that pre-onset encoding is purely a signature of predictive pre-activation, then decorrelating the pre- and post-onset brain responses should effectively remove that signature. The fact that pre-onset encoding remains largely intact after this procedure suggests that our initial premise was false; the observed pre-onset encoding is likely not a signature of pre-activation. We would also like to note that in this analysis, we use both residualized neural data and we use decorrelated embeddings. Therefore, the majority of stimulus dependencies are removed. Nevertheless, as the reviewer notes, some dependencies such as bi-grams and other word-co-occurrences, inevitably remain. These dependencies might explain the remaining pre-onset encoding we observed. This aligns with our main message of the paper. In the revisions, will provide a detailed description of the decorrelation process and we will make this interpretive logic more explicit in the main text.

Reviewer 3:

We are grateful for the reviewer’s detailed comments and for raising several points that will significantly improve the clarity and comparability of our study. Specifically, the reviewer’s feedback helped us realize that our evidence for postdiction required further clarification. While the encoding of the immediate preceding word ($d-1$) may involve recognition lags, we observe that word $d-2$ further improves the brain score even after the current word's onset, beyond what is explained by word $d-1$ alone. This may extend beyond simple recognition delays. To address this we will visualize this effect further in the upcoming version and expand the manuscript to include alternative explanations for this observation, such as extended lexical processing or integration delays.

To ensure our results are not biased toward high-frequency or function words, we will re-run our analyses including multi-token words. Given that these words constitute a small part of the datasets, we expect our core findings to remain stable.

In line with our response to reviewer 2, we will more clearly emphasize that despite our extensive controls, we cannot be sure that we accounted for all regularities inherent to natural speech.

Additionally, we will increase the context windows of the LLM to match the larger windows used in previous literature and add significance tests, error bars, and noise floor indications to our figures to ensure the reliability and variability of our findings are clearly communicated.

eLife Assessment

The authors developed and validated a gut-on-chip system to mimic the gut environment for studies of Clostridioides difficile infection in vitro. Although the data generated is useful to the field, the evidence provided to support the conclusions is incomplete. Methodology that is not complete, as well as discrepancies regarding the proposed mode of action of lipoxin A4, are significant weaknesses.

Reviewer #1 (Public review):

Summary:

This study investigates the potential for the immune mediator, lipoxin A4 (LXA4), to alleviate inflammation/damage caused by the healthcare-associated pathogen, Clostridioides difficile. Using both a novel in vitro "gut-on-a-chip" system and a murine model of disease, the authors demonstrate potential disease attenuation by LXA4. Specifically, LXA4 at select administration times during development of C. difficile infection (CDI) may upregulate markers associated with intestinal barrier integrity (ZO-1) and attenuate immune markers typically associated with inflammation (IL-8, IFN-γ, etc.). Overall strengths of the study include the establishment of a novel in vitro model that incorporates anaerobic and aerobic environmental conditions of the gut, as well as some results suggesting a potential role for LXA4 in modulating CDI. However, critical weaknesses of the manuscript, including incomplete methods and a lack of some critical controls or measurements, lead to only partial support for the authors' conclusions. Collectively, the data suggest alternate potential (and perhaps more likely) mechanisms by which LXA4 might modulate CDI. Specific strengths and weaknesses are listed below.

Strengths:

(1) A major strength of the study is the use and description of the gastight, gut-on-a-chip system that allows for co-culture of host cells (with aerobic needs) with anaerobic bacteria. While perhaps this (and other in vitro) system does not exactly "more accurately recapitulate specific host-microbe interactions (line 82)", integration of oxic and anoxic conditions that recapitulate the gut is indeed difficult to incorporate in vitro. Results surrounding C. difficile and Caco-2 cell viability in the described system seem substantiated.

(2) Assessing LXA4 in both an in vitro and in vivo (mouse) model is a complementary strategy. Results from both experiments seem to support the observation that LXA4 can possibly attenuate C. difficile.

(3) Overall, the manuscript is well-written and straightforward (albeit lacking in some details-see below).

Weaknesses:

(1) A major weakness of the manuscript in its current state is that the methods are incomplete or unclear. Details on how C. difficile was handled (strain info, preparation in experiments, quantification) are lacking. Mouse model information (inoculation, housing, number of animals) is missing, particularly for the second set of mouse experiments, which is not described at all in the methods. An IACUC or similar statement is not included.

a) For in vitro experiments, how exactly were C. difficile quantified using flow cytometry? This is not exactly clear in the methods or the results, where C. difficile counts are referred to as 'normalized' without specific units (Figure 1D). What are these counts normalized to? How much of the total effluent was measured? This might also explain the discrepancy in C. difficile counts, referred to below.

b) How exactly were C. difficile quantified for the mouse studies? The authors state that fecal samples were plated on CCFA agar, but the y-axis merely states "numbers of bacteria". Other bacteria grow on CCFA. How were C difficile specifically enumerated?

c) Figure 4. For the vancomycin / LXA4 experiments, were mice subjected to antibiotics to render them initially susceptible to C. difficile? If so, this should be included in experimental timelines. If not, how do the investigators know that mice were colonized with C. difficile in each instance (usually mice require abx perturbation for susceptibility)? How was vancomycin administered to mice? In any case, C. difficile loads should be quantified for all conditions in these experiments.

d) Related to the above (Figure 4 experiments), were all of these measurements taken only 24 hours post-infection? These experiments are not described well in the results and are not described at all in the methods.

e) How many total mice were included in the study groups, and how were they housed? Cage effects can influence any mouse study, but are especially important in CDI studies, given the importance of the microbiome in the development of CDI.

f) How were mice inoculated with C. difficile? Was this a spore or vegetative inoculum, and how? The state inoculum of 1x10^-9 is quite large.

g) What is the history/ribotype of the C. difficile strain (1482?) used in all the experiments? How does this compare to other commonly used strains of C. difficile? Different strains demonstrate overall virulence, disease dynamics, and disease severity in animal and in vitro models.

(2) Related to some methodological clarifications, there are some missing controls that would bolster support for final interpretations and some odd discrepancies in the study that are not explained.

a) Figure 1C: How does the mucin layer (i.e., Caco-2 cell differentiation) look under anoxic conditions? This measurement was only included in the oxic conditions.

b) In initial C. difficile quantification within the system (Figure 1D), C. difficile counts seem to range from 3 - 12 (undefined units). In the C. difficile / LXA4 experiments, these counts only reach ~1.8 (undefined units) in the CDI group. What explains this large discrepancy? Furthermore, the prophylactic LXA4 group seems to hover around < 0.5, similar to what is seen at 0 or 3 hours with C. difficile alone. This suggests that C. difficile might not proliferate at all in the presence of LXA4, perhaps explaining why epithelial barrier functions and immune attenuation are improved.

c) Figure 2B. What do untreated controls (no CDI, but with or without LX4A) look like compared to the experimental groups? These controls should be included with the main Figure 2 results.

d) If all metrics in Figure 4 were measured only 24 hours after infection, this is a VERY short timeline for CDI. Depending on the strain, damage might not even be quantifiable by this time point. For instance, C. difficile 630 disease signs only appear 2-4 days post-infection. C. difficile VPI kills mice within 36 hours, but Figure 3 results suggest that mice survive just fine. What is known about this strain's disease dynamics in mice? Alternatively, is it possible that LXA4 alone increases barrier integrity / attenuates inflammation? The inclusion of non-CDI controls (with or without abx; untreated; etc) might help distinguish this.

(3) Perhaps the largest weakness of the manuscript is the interpretation of how LXA4 might attenuate CDI, which is also misleading as a title. The authors purport that disease attenuation is via LXA4, increasing barrier integrity and attenuating inflammation. However, much of the evidence suggests that LXA4 might limit C. difficile colonization. If there is less C. difficile (thus less toxin) in any system, all aspects of the disease will be attenuated. Indeed, their data suggest that there are decreasing amounts of C. difficile in the presence of LXA4, which could be due to direct inhibition of C. difficile or its toxin, removing nutrients necessary for C. difficile growth, or indirect effects on microbes in the gut environment (in mice). Proper quantification of C. difficile, toxin measurements, and dose responses would better distinguish which mechanism is more likely.

a) The initial LXA4 experiments assessing potential therapeutic effects (mainly Figure 2) were conducted at 6 hours post-infection. What is the C. difficile load and/or toxin burden at this time? In some ways, LXA4 administration at this time point could also be thought of as 'prophylactic', given that damage (and maybe C. difficile virulence?) has not occurred yet.

b) Is it possible that LX4A administration prior to C. difficile inoculation influences C. difficile physiology (colonization; toxin production), rather than alleviating C. difficile damage? C. difficile colonization should be quantified in all the LX4A experiments (only a subset is shown in Figure 2).

c) Line 213 / Figure 2G. While it is possible that "LXA4 reprograms the intestinal epithelial transcriptome to bolster barrier function and temper immune signaling", the decreased C. difficile measurements in the presence of LXA4 suggest it impacts C. difficile colonization / function. This decreased level of C. difficile (and thus less toxin) could also explain immune response attenuation. Toxin measurements, as well as some C. difficile dose responses within the system, could help distinguish which possibility is more likely.

d) Both in vitro and in vivo experimental results suggest a prophylactic role for LXA4 in CDI. However, the current experiments cannot distinguish whether this prophylactic response is due to host-specific anti-inflammatory attenuation (which the authors suggest) or due to an impact on C. difficile colonization/function (which is not acknowledged). The effect of LXA4 on C. difficile could be via direct inhibition of C. difficile growth or host remodeling that modulates C. difficile colonization or metabolism.

e) Figure 4. While the data seem to support some preservation of barrier function and attenuation of inflammatory responses, this could once again be due to delaying, decreasing, or inhibiting C. difficile colonization itself, rather than attenuation by LXA4. Indeed, vancomycin-induced improvements within this short amount of time are likely due to inhibiting C. difficile, as it is an antibiotic used to directly kill C. difficile.

(4) Other comments:

a) Given that the current results cannot preclude alternate, if not more likely, explanations for how LXA4 might attenuate CDI, the manuscript should include a more comprehensive discussion. This could include study caveats, C. difficile-specific context about infection (i.e., infection dynamics, context with other experiments).

b) Dysbiosis: undefined definition, as this is context-dependent. For CDI, what does this mean?

c) Unclear if in vitro intestinal models "more accurately recapitulate specific host-microbe interactions", even considering caveats of animal models. Rather, each model has their own purpose; I would be careful about this phrasing (line 82).

d) Line 86: not just "thrives under strict anaerobic conditions", but is necessary for growth. C. difficile is an obligate anaerobe.

Reviewer #2 (Public review):

C. difficile infection (CDI) is one of the most common nosocomial intestinal infections with a high rate of disease recurrence. Importantly, antibiotics used to treat CDI are a double-edged sword because disruption of the gut microbiome also increases the susceptibility to CDI. Therefore, there is an unmet need for alternative therapeutic approaches against CDI. CDI pathogenesis is initiated by the cytotoxic toxins TcdA and TcdB that target and induce cell death of intestinal epithelial cells, leading to epithelial barrier breakdown and inflammation. Innate immune cells such as neutrophils and innate lymphoid cells (ILCs) were shown to be crucial to control CDI during the acute phase. Based on previous reports that the pro-resolving mediator Lipoxin A4 (LXA4) inhibits neutrophil infiltration and promotes efferocytosis as well as mucosal repair, the authors reason that LXA4 could be leveraged as a therapy against CDI.

The authors developed and validated a gut-on-chip (GOC) system to mimic the gut environment for C. difficile infection in vitro studies. LXA4 was able to decrease C. difficile-induced inflammation only when used as a prevention but not as a therapy. IEC RNA-seq revealed that LXA4 treatment upregulates a transcriptional program that reinforces barrier function. These data were replicated in an in vivo model of CDI. Overall, the study provides evidence that LXA4 could be repurposed for CDI treatment, but some claims are not fully supported by the data, such as the synergy between LXA4 and vancomycin, which has not been experimentally tested in vivo.

Author response:

Public Reviews:

Reviewer #1 (Public review):

(1) Completeness and clarity of Methods (Weakness #1).

We will substantially expand the Methods section to include:

(a) Detailed information on C. difficile strain ribotype 1382 (correcting the typographical error "1482"), including its virulence characteristics, toxin production dynamics, and rationale for its selection.

(b) Step-by-step protocols for on-chip bacterial quantification by flow cytometry, including sample collection volume, processing, and the specific normalization procedure (with clarification that normalized values are intended for within-experiment comparisons only).

(c) Full description of mouse experiments: antibiotic pre-treatment regimen, inoculation details (spores vs. vegetative cells, justification of the 1×10^9 CFU dose), animal numbers, housing conditions, and cage-effect considerations. The IACUC approval statement will be moved from Acknowledgments to Methods.

(2) Mucin layer characterization under anoxia (Weakness #2a).

We will clarify in the Methods that mucin staining was performed after the initial oxic culture phase to confirm differentiation prior to anaerobic challenge. We will cite relevant literature discussing the stability of pre-formed mucin layers under short-term anoxic conditions and incorporate this discussion to contextualize our experimental design in the revised Methods.

(3) Discrepancy in C. difficile counts and mechanism of LXA4 action (Weakness #2b, #3).

We will provide a detailed explanation of our flow cytometry normalization algorithm, emphasizing that values are only comparable within a given experimental batch. We plan to perform additional in vitro experiments to directly assess the effect of LXA4 on bacterial growth and toxin secretion. These data will help distinguish between direct antibacterial effects and host-mediated protection, and the revised Discussion will incorporate this analysis.

(4) Missing controls and experimental timelines (Weakness #2c–d).

We will clarify that Figure 4 presents gut-on-chip experiments, not animal studies. The corresponding methods will be fully described. Additionally, we will include cross-experiment alignment analyses (using the CDI group as a common reference) to integrate negative control data from separate experimental batches. We also plan to generate additional data examining the effect of LXA4 alone (without infection) on epithelial barrier integrity and inflammatory status, which will be included as supplementary controls.

(5) C. difficile strain characterization (Weakness #1g).

A comprehensive section on ribotype 1382 will be added to the Methods, detailing its in vitro growth kinetics, toxin production profiles, and disease dynamics in the murine model, with appropriate literature citations.

(6) Dysbiosis definition and phrasing adjustments (Other comments #b–d).

We will revise the text to provide a clear definition of dysbiosis in the context of CDI. We will also temper the phrasing in line 82 to more accurately describe the advantages of our GOC system relative to other in vitro models, and correct the description of C. difficile as an obligate anaerobe.

Reviewer #2 (Public review):

(1) Synergy between LXA4 and vancomycin in vivo.

We agree that the synergistic effect observed in the GOC model requires validation in an animal model. We are currently conducting mouse experiments to test the combination of prophylactic LXA4 with vancomycin treatment. The results will be included as a new Figure 5 in the revised manuscript.

We are confident that these planned revisions will fully address the reviewers' concerns and significantly enhance the rigor and impact of our study.

eLife Assessment

This fundamental study describes long-range serial dependence of performance on a visual texture discrimination training task that manipulated conditions to induce differing degrees of location transfer of learning. The authors re-analyzed previously-published, behavioral data, generating compelling evidence from converging approaches that the serial dependence effects persist over multiple days of training, and may share a common causal mechanism with training-induced location transfer. By informing our understanding of the importance of temporal integration to long-term perceptual learning and its propensity towards specificity or generalizability, these results should interest neuroscientists who seek to uncover underlying neural mechanisms for these processes.

Reviewer #1 (Public review):

This paper presents a reanalysis of a large existing dataset to examine whether serial dependence effects-systematic influences of recent stimulus history on current perceptual judgments-are associated with generalization in perceptual learning. The central hypothesis is that extended, longer-range history effects (beyond the most recent trials) are beneficial for transfer across locations. The authors reanalyze data from a texture discrimination task in which observers discriminated peripheral target orientation against a line background, with performance quantified by stimulus-onset asynchrony thresholds. Three training conditions were compared: a fixed single-location condition, a two-location alternating condition, and a dummy-trial condition with frequent target-absent trials. Transfer was assessed after training at new locations. Serial dependence was quantified using history-sequence analyses and linear mixed-effects models estimating bias weights across stimulus lags, with summary measures distinguishing recent (1-3 trials back) and more distant (4-6 trials back) dependencies.

The authors report extended serial dependence effects, persisting up to 6-10 trials back, with substantial cumulative bias that remains stable across multiple days of training and is not correlated with overall performance thresholds. Recent history effects are stronger for faster responses, suggesting a contribution from decision- or response-related processes, whereas more distant effects decline within sessions, potentially reflecting adaptation dynamics. Critically, longer-range serial dependence is significantly stronger in training conditions that promote generalization than in the single-location condition. Individual differences in the strength and decay profile of distant history effects predict the magnitude of transfer across locations, whereas recent history effects do not. History effects are also correlated across trained locations, suggesting stable individual differences.

The authors interpret longer-range serial dependence as reflecting integrative processes that extract task-relevant structure over time, thereby supporting generalization, while shorter-range effects are attributed to more transient mechanisms such as priming or decision-level bias. The discussion connects these findings to Bayesian accounts of perceptual stability and to concepts of overfitting in machine learning.

The study offers a novel and thoughtful link between short-term serial dependence and long-term generalization in perceptual learning, helping bridge two literatures that are often treated separately. The large dataset enables robust estimation of individual differences, and the use of mixed-effects modeling appropriately accounts for variability across observers. The empirical distinction between recent and more distant history effects is well-supported and adds important nuance to interpretations of serial dependence. Converging evidence from both group-level comparisons and individual-level correlations strengthens the central conclusions.

Comments on revisions:

The authors have effectively addressed my concerns. The new robustness analyses (Supp. Fig. S3), supplementary toy model, clearer DDM-based mechanistic distinctions, and expanded discussion of limitations and generality fully resolve my original points.

Reviewer #3 (Public review):

Summary:

This reanalysis of a classic study of visual perceptual learning in a texture discrimination task convincingly demonstrates the presence of sequential dependence effects, commonly seen in response time analyses in 2-alternative tasks, on response accuracy in the texture task in visual periphery and in a simultaneous central letter report at fixation. Overall, this paper provides a new and interesting analysis of the effects of sequential dependencies from trial to trial on performance, learning, and generalizability in perceptual learning.

Strengths:

This new analysis of sequential dependency effects (SDEs) extends commonly observed sequential effects in two-choice reaction times to accuracy and relates them to response accuracy during visual learning in a frequently used perceptual learning task. The paper makes a convincing case that different conditions known to impact generalization of learning to a second visual location also expresses quantitatively distinct n-back SDEs.

Weaknesses:

Additional analyses now back up the analysis of effects of SDEs using trials selected to enhance the size of the effects, specifically when the current trial is low visibility and the prior trial is of high visibility. The authors now provide a practical analytic reason for this choice.

Comments on revisions:

The revision has successfully addressed comments in the original reviews.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This paper presents a reanalysis of a large existing dataset to examine whether serial dependence effects-systematic influences of recent stimulus history on current perceptual judgments-are associated with generalization in perceptual learning. The central hypothesis is that extended, longer-range history effects (beyond the most recent trials) are beneficial for transfer across locations. The authors re analyze data from a texture discrimination task in which observers discriminated peripheral target orientation against a line background, with performance quantified by stimulus-onset asynchrony thresholds. Three training conditions were compared: a fixed single location condition, a two-location alternating condition, and a dummy-trial condition with frequent target-absent trials. Transfer was assessed after training at new locations. Serial dependence was quantified using history-sequence analyses and linear mixed effects models estimating bias weights across stimulus lags, with summary measures distinguishing recent (1-3 trials back) and more distant (4-6 trials back) dependencies.

The authors report extended serial dependence effects, persisting up to 6-10 trials back, with substantial cumulative bias that remains stable across multiple days of training and is not correlated with overall performance thresholds. Recent history effects are stronger for faster responses, suggesting a contribution from decision- or responserelated processes, whereas more distant effects decline within sessions, potentially reflecting adaptation dynamics. Critically, longer-range serial dependence is significantly stronger in training conditions that promote generalization than in the single-location condition. Individual differences in the strength and decay profile of distant history effects predict the magnitude of transfer across locations, whereas recent history effects do not. History effects are also correlated across trained locations, suggesting stable individual differences.

The authors interpret longer-range serial dependence as reflecting integrative processes that extract task-relevant structure over time, thereby supporting generalization, while shorter-range effects are attributed to more transient mechanisms such as priming or decision-level bias. The discussion connects these findings to Bayesian accounts of perceptual stability and to concepts of overfitting in machine learning.

The study offers a novel and thoughtful link between short-term serial dependence and long-term generalization in perceptual learning, helping bridge two literatures that are often treated separately. The large dataset enables robust estimation of individual differences, and the use of mixed-effects modeling appropriately accounts for variability across observers. The empirical distinction between recent and more distant history effects is well-supported and adds important nuance to interpretations of serial dependence. Converging evidence from both group-level comparisons and individuallevel correlations strengthens the central conclusions.

Several limitations should be addressed. First, the study relies entirely on previously collected data, without experimental manipulations designed to selectively isolate serial dependence mechanisms. Filtering choices, while theoretically motivated, may amplify history effects in ways that are difficult to quantify. Second, sequential dependencies can arise from multiple sources, including gradual updating of internal weight structures, adaptation processes, and history-dependent biases in decisionmaking. The current analyses do not clearly separate these contributions, limiting mechanistic attribution of long-range effects. Third, the conclusions are based on a single perceptual task, leaving open questions about generality across paradigms. Finally, while the discussion references computational ideas, no explicit modeling is provided to test whether plausible learning rules can jointly account for the observed history profiles and transfer effects.

We now address these issues in the manuscript (see below for detailed responses) and provide a toy model (supplementary material) where the observed effects are explained by simple learning mechanisms.

The findings align with theoretical frameworks that conceptualize perceptual learning as gradual reweighting of stable sensory representations at the decision stage (e.g., Petrov et al., 2005). Trial-by-trial updates in these models naturally give rise to sequential dependencies and sensitivity to training statistics. The observation that longer-range history effects predict generalization is consistent with broader temporal integration supporting more flexible learning, while narrower integration may lead to specificity. The results also indicate that multiple mechanisms - including decisionlevel biases and adaptation - may coexist with reweighting processes, highlighting the value of hybrid accounts.

In summary, this is a careful and data-rich reanalysis that highlights a potentially important role for serial dependence in enabling generalization during perceptual learning. While the underlying mechanisms remain underspecified, the evidence supporting the reported associations is strong, and the work provides a valuable empirical foundation for further experimental and modeling efforts.

Reviewer #2 (Public review):

This manuscript investigates how people's perceptual reports are influenced by events and trials in the past, and how this long-range dependence relates to broader learning across locations in a visual learning task. The authors present clear and internally consistent analyses showing that extended temporal integration is associated with greater generalization of learning. The study is thought-provoking and may contribute meaningfully to understanding how short-term influences and long-term improvement interact, although several interpretational points would benefit from clarification.

Strengths:

(1) The manuscript identifies unusually long-range perceptual biases extending up to ten trials back, which is a striking and potentially important finding.

(2) The association between strong long-range dependence and greater learning generalization is clearly documented and supported by consistent analyses.

(3) The dataset is large and rich, and the authors apply repeated and well-controlled analyses that give confidence in the stability of the effects.

(4) The writing is generally clear, and the manuscript raises interesting conceptual links between temporal integration and generalization of learning.

Weaknesses / Points Requiring Clarification:

(1) The manuscript repeatedly equates generalization with increased efficiency, but this relationship is not universally true. In some populations or tasks, excessive generalization can reduce task-specific efficiency. The authors should discuss this context-dependence to clarify when generalization is beneficial versus detrimental.

We agree with the reviewer that generalization does not strictly imply increased efficiency; in some contexts, over-generalization can indeed be detrimental. We now explicitly note in the Introduction that serial dependence can impair performance when stimuli vary randomly across trials. We have reviewed the manuscript to ensure we do not explicitly equate generalization with efficiency. Our argument is specifically that long-range SDEs support the transfer of learning (generalization).

(2) Serial dependence is also present, though smaller, in the central fixation task. It remains unclear whether this bias could contribute to the serial dependence observed in the main task. The authors should clarify whether the two biases are independent or whether the central-task bias might partially influence orientation judgments in the main task.

These two tasks are independent, one requires T/L discrimination the other V/H discrimination. See our detailed response below.

(3) Several figure captions and labels contain minor inconsistencies in formatting and terminology. Careful proofreading would improve clarity.

We thank the reviewer for pointing this out and have proofread the captions to improve formatting and terminology consistency throughout.

Reviewer #3 (Public review):

This reanalysis of a classic study of visual perceptual learning in a texture discrimination task convincingly demonstrates the presence of sequential dependence effects, commonly seen in response time analyses in 2-alternative tasks, on response accuracy in the texture task in the visual periphery and in a simultaneous central letter report at fixation. Overall, this paper provides a new and interesting analysis of the effects of sequential dependencies from trial to trial on performance, learning, and generalizability in perceptual learning.

Strengths:

This new analysis of sequential dependency effects (SDEs) extends commonly observed sequential effects in two-choice reaction times to accuracy and relates them to response accuracy during visual learning in a frequently used perceptual learning task. The paper makes a convincing case that different conditions known to impact generalization of learning to a second visual location also express quantitatively distinct n-back SDEs.

Weaknesses:

Most of the new analyses emphasize the effects of SDEs, including trials designed to enhance the size of the effects, specifically when the current trial is low visibility, and the prior trial is of high visibility. Unless there is an argument that learning and subsequent generalization primarily occur in low-visibility trials, the presentation should also include displays and an emphasized discussion of analysis for all trials, unfiltered.

We analyze effects on close to threshold (small-medium SOA) current targets preceded by above threshold (high SOA) reference targets. This is motivated by both technical issues and theoretical assumptions. In psychophysics, when using percent correct as a measure of performance, bias cannot be reliably estimated at or near ceiling performance, as correct responses leave little room for bias to manifest. Regarding the ‘easy’ targets used as a reference, having them at low SOA introduces uncertainty as for the reference orientation against which bias is measured, with their perceptual effect being ambiguous. Theoretically, we note that in perceptual learning with threshold targets, the introduction of clear targets in the absence of feedback enables learning (see Discussion, where we added: 'Most interestingly, in our experiments without feedback on the texture task, the experimental conditions yielding the strongest bias were also found to enhance learning in the absence of feedback (Liu et al., 2012)')

We have addressed this concern also by conducting additional robustness analyses with unfiltered prior-trial history. We analyzed data without the prior-visibility filter; results are presented in a new Supplementary Figure S3 and confirm our main findings (see addition to Methods: "Finally, to verify that our findings are not artifacts of these filtering choices, we also conducted control analyses including all prior-trial history regardless of visibility; these results are presented in Supplementary Figure S3 and confirm the robustness of our main findings.").

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) How manipulations of stimulus statistics, uncertainty, or feedback could selectively engage different forms of serial dependence

We expect serial dependence to be modulated by all these parameters. In classical SDT, stimulus statistics are known to affect response bias, as are temporal correlations in stimulation sequences. We note in the manuscript that we employed random sequences (50% chance for V and 50% for H targets), eliminating expectation-based biases toward either orientation. Stimulus uncertainty is known to increase serial dependence, as we also found here. Feedback is also expected to have an effect, the literature is somewhat ambiguous about this, but this may also depend on experimental design. We note that the main task studied here (TDT) had no feedback while the central T/L task did have feedback, both showing serial dependencies. In the manuscript we point to reviews of SDE where much of this is discussed.

(2) How explicit computational models could help distinguish decision bias from structural learning

We use the drift diffusion model (DDM) to distinguish decision bias (starting point in DDM) from structural learning (changes in drift rate). DDM predicts that decision bias is short lived, mainly affects fast reaction times (RT) while biases due to drift rate asymmetry persists to long RTs. We present these results in Figure 3.

(3) Whether similar relationships are observed in other perceptual domains

We are not aware of any other study linking serial dependence and perceptual learning or reporting such a link. We expect the link between long-range serial dependence and learning generalization to extend beyond the TDT (see new paragraph in Discussion). We hope this framework will motivate similar analysis in other labs where comparable datasets exist.

(4) How sensitive are the results to the filtering choices used in the analysis?

We analyze effects on close to threshold (small-medium SOA) current targets preceded by above threshold (high SOA) reference targets. This is motivated by both technical issues and theoretical assumptions. In psychophysics, when using percent correct as a measure of performance, bias cannot be reliably estimated at or near ceiling performance, as correct responses leave little room for bias to manifest. Regarding the ‘easy’ targets used as a reference, having them at low SOA introduces uncertainty as for the reference orientation against which bias is measured, with their perceptual effect being ambiguous. Theoretically, we note that in perceptual learning with threshold targets, the introduction of clear targets in the absence of feedback enables learning (see Discussion, where we added: 'Most interestingly, in our experiments without feedback on the texture task, the experimental conditions yielding the strongest bias were also found to enhance learning in the absence of feedback (Liu et al., 2012)')

We have addressed this concern also by conducting additional robustness analyses with unfiltered prior-trial history. We analyzed data without the prior-visibility filter; results are presented in a new Supplementary Figure S3 and confirm our main findings (see addition to Methods: "Finally, to verify that our findings are not artifacts of these filtering choices, we also conducted control analyses including all prior-trial history regardless of visibility; these results are presented in Supplementary Figure S3 and confirm the robustness of our main findings.").

Reviewer #2 (Recommendations for the authors):

(1) Clarify mechanisms underlying long-range serial dependence. Please better distinguish possible sources of serial dependence (e.g., decision bias, adaptation, reweighting) and clarify which interpretations are supported or remain ambiguous given the current analyses

Our manuscript discusses the mechanisms underlying the dissociation between recent and distant SDEs in the Discussion section. Specifically, we report that:

Recent SDEs are RT-dependent (stronger with faster responses) consistent with decision-level criterion shifts (Dekel & Sagi, 2020)

Distant SDEs are RT-independent consistent with neural reweighting/template updating

We also discuss the role of sensory adaptation in truncating long-range integration, supported by within-session decline of SDEs, reduced distant SDEs in the 1loc condition, and the original findings by Harris et al. (2012).

We have added an explicit acknowledgment that our correlational approach cannot definitively establish causality (see addition to Discussion: "While these converging findings support distinct mechanisms for recent and distant SDEs, our correlational approach cannot definitively establish causality, and targeted experimental manipulations would further strengthen these interpretations.").

(2) Test robustness to analytic choices

We have conducted robustness analyses by removing the prior-trial visibility filter. The results are presented in a new Supplementary Figure S3 and confirm that our key findings remain qualitatively unchanged (see addition to Methods referencing Supplementary Figure S3).

(3) Strengthen the computational link

We have expanded the Discussion to reference relevant computational models and specify predictions for future modeling work. We now cite Petrov et al. (2005). We provide a toy model implementing trial-by-trial template update that show SDE that is correlated with learning transfer. Importantly, in this model, long range SDE is a consequence of learning dynamics (see new paragraph in Discussion, and model simulation in supplementary material).

(4) Discuss generality and experimental tests. Briefly address whether similar effects are expected across other tasks or sensory domains, and outline experimental manipulations that could causally test the role of serial dependence in generalization.

We have added discussion of generality across perceptual domains and outlined the prediction that future work could test the SDE-generalization link in other tasks where both phenomena have been documented (see new paragraph in Discussion).

Reviewer #2 (Public Review - Point 2): Central task SDE independence

The SDEs observed in the central letter task and peripheral TDT are likely independent, as they involve different stimulus features (letter identity vs. orientation), different response mappings, and show distinct performance patterns across conditions. The absence of condition differences in central-task SDEs (described in the Results section under "SDE differences between conditions" end of paragraph), despite robust differences in TDT SDEs, further suggests that the peripheral orientation biases are not contaminated by central-task response tendencies. Note that the central task was fixed across conditions, stayed at fixation when location was changed, and when dummy trials were presented.

Reviewer #3 (Recommendations for the authors):

(1) Reference to Falmagne, Cohen, & Dwivedi (1975)

We have added this reference to the Introduction, acknowledging the historical foundation of sequential effects in perceptual decisions

(2) The SDE data of Figure 1 are (per the figure legend) from the 1 loc data of Harris et al., "pooled over all testing days", and filtered for trials with low-visibility current targets (SOA < SOA-threshold+20ms). Specify whether this threshold criterion is on a per-subject basis. State in the legend that "all testing days" includes Days 1-8 (4 days with the first location and another 4 days testing generalization to a second location).

We have revised the Figure 1 legend to clarify:

"Days 1–8; 4 days at the first location and 4 days at the second location to assess generalization"

"calculated on a per-subject basis"

(3) The leadup emphasizes that the analysis in the figure emphasizes trials where the effect is expected to be as large as possible (cited as 40 +/- 3%), while visible current targets (at n) biases were 5+/-1%.

See below, after (4).

(4) Unless a theoretical position associates learning just with low visibility (if so, explain), consider including two other panels showing the sequential dependencies for all trials, and the linear model weights over the last 10 trials for all trials.

We acknowledge that the main analyses emphasize conditions that maximize SDE expression. To verify robustness, we conducted control analyses including all prior-trial history regardless of visibility; these results are presented in Supplementary Figure S3 and confirm our main findings.

There are both theoretical and technical justifications for the filtering applied:

It is well known that learning, in particular without feedback (as in our TDT), is facilitated by a mixture of threshold level stimuli and suprathreshold easy trials (e.g., Liu et al., 2012).

Technically, it is impossible to measure bias with highly discriminable stimuli where performance is perfect or close to it, thus such trials are expected to dilute the measured effect. On the other hand, when considering serial effects from low sensitivity trials, we face an uncertainty involved in defining the actual orientation relative to which the bias needs to be computed.

(5) Figure S1 seems to indicate that average thresholds over all days (location 1 and location 2) are unrelated to the sequential dependence across subjects and that the amount of learning in location 1 is unrelated to the sequential dependencies across subjects in all the varied conditions. Since Figure S1 includes all 50 subjects, it includes some conditions with dummy trials interspersed. Clarify in the description whether the dummy trials are ignored for the purposes of the SDE analyses.

We have clarified in the Methods how trials are handled in the analysis: "To preserve the precise temporal structure of the data, all trials were included in the sequential n-back count across all experimental conditions, thus dummy trials were counted as time bins but their contribution was ignored. In the Linear Mixed Effects (LME) analysis, we modeled these trial types using distinct regressors: each n-back lag included separate predictors for visible and invisible targets, further differentiated by trial type (dummy vs. target) and relative location (ipsilateral vs. contralateral) where applicable. The SDE values reported here reflect only the influence of relevant target-present history trials; the effects of other history types (e.g., dummy trials), while estimated to ensure the temporal integrity of the model, are not presented."

(6) The conclusion from this analysis seems to be that the overall average threshold and the amount of initial learning are both uncorrelated with the strength of sequential dependencies across subjects. This conclusion should be added to the description in the main paper.

This finding is now discussed in the Discussion section, referring to the main Results section [ No significant correlation was found between biases and SOA thresholds across observers (r = -0.13, p = 0.37, average across days 1-8), nor between biases and improvements in performance at the first location (r = -0.09, p = 0.54, average across days 1-4), suggesting that the magnitude of serial dependence does not predict the overall amount of perceptual learning (Supplementary Figure S1)].

(7) Decay of SDE section clarifications

We have made the following clarifications:

RT definition: Added to Methods: "The reaction time (RT) used in the analysis was defined as RT(TDT) – RT (fixation task), where RT for each task was measured from stimulus onset."

N-back counting: Clarified in Methods (see response to point 5 above): all trials were included in the chronological sequence; the LME analysis assigned separate predictors at each lag for visible/invisible targets and for trial categories (dummy vs. target) and locations (ipsilateral vs. contralateral). The results reported do not include effects of dummy trial, except where response dependent SDE was reported (Fig 2a, SDE for response key).

2loc n-back effect: The longer-range effects in the 2loc condition likely reflect reduced adaptation allowing longer temporal integration, combined with the location-selective nature of SDEs.

RT and mechanism interpretation: The manuscript discusses that the critical observation is the qualitative difference in RT sensitivity between recent and distant SDEs, consistent with the drift-diffusion framework where criterion shifts are RTdependent while drift bias is RT-independent (Dekel & Sagi, 2020). We have added an acknowledgment of the correlational limitations of this interpretation.

Moving figures to supplement: We prefer to keep Figures 4 and 5 in the main text as they document important dynamics supporting our mechanistic interpretation.

eLife Assessment

This study presents important findings that bovine mammary epithelial cells can be infected with both avian and human influenza A viruses, providing a potential site for viral reassortment. The evidence to support these claims is generally solid; however, the evidence suggesting lower permissiveness of cells from other organs is incomplete. The work will be of interest to virologists and evolutionary biologists working on cross-species transmission of viruses and pandemic preparedness.

Reviewer #1 (Public review):

Summary:

Here, Pinto and colleagues set out to investigate whether the cow udder is a potential mixing site for the influenza virus. The authors have demonstrated that bovine mammary epithelial cells can be infected with both avian and human influenza A viruses, supporting the idea that the cow udder may be a potential site for reassortment. Furthermore, they demonstrate that the bovine-adapted IAV replicates to similar titers in avian epithelial cells when compared to an AIV precursor virus. Thus, suggesting there is no fitness trade-off, and confirms the potential for spill-back of the cattle B3.13 into poultry, which has already been observed. Overall, I believe the authors achieved their aims. However, there are instances in which the results do not entirely support the conclusions (noted in weaknesses). Given the ongoing questions surrounding highly pathogenic avian influenza A virus in dairy cows, this work provides valuable evidence for the potential of the cow udder as a site of reassortment. These findings highlight the need for surveillance of influenza A virus incursions into livestock species, particularly cows. Some specific strengths and questions regarding weaknesses have been outlined below.

Strengths:

(1) The authors use a diverse range of cell types and influenza A virus strains, as well as a wide range of techniques to address the questions at hand.

(2) The use of cells from multiple bovine breeds for the MAC-T, bMEC and explants suggests the phenomenon is not unique to a single breed.

(3) The results suggesting there is no fitness trade-off for Cattle Texas in an avian host are interesting, and confirm the potential for spill-back of the cattle B3.13 into poultry, which has been observed.

Weaknesses:

I have listed my complete questions/concerns below. However, there are two main weaknesses of the article in its current state. Firstly, there is no apples-to-apples comparison in terms of determining a preference for IAV to infect the cow udder over other organs (Q4). The mammary gland and respiratory tract are represented by epithelial cells, but for other organs, fibroblasts were chosen. I think the fairer comparison would be to compare epithelial cells from different organs to demonstrate a preference for the mammary gland. Secondly, the main premise of the article relies on bMEC and MAC-T (primary and immortalised mammary epithelial cells), facilitating higher viral growth than the cells from other organs. Yet throughout the article, a 10x higher dose of IAV is used in the bMEC cells compared to everything else (Q6). This raises the question of how much of the results are due to a preference for the mammary epithelial cells, and how much is simply due to the increased dose.

Reviewer #2 (Public review):

The authors use a library of influenza A viruses from different strains, classified in lab-adapted, human, avian, and swine according to the animal from which they were isolated. They propose that the cow mammary gland serves as a mixing vessel for influenza A viruses. As a first approach, the authors assess susceptibility to infection across different cell types, including continuous and primary cell lines, bovine mammary cells, and mammary explants. All these cells support polymerase activity. Then, they analyzed changes in the bovine virus's viral fitness relative to an avian precursor. The authors use single-gene replacement to study whether and which RNP segments improve viral transcription. As part of this section, they also test IFN-specific antagonism by NS1 to assess the input of segment 8. Quantitative glycomic analysis was performed on the continuous bovine mammary cell line to demonstrate the presence of both a2,3 and a2,6, which is consistent with their observation that these cells can be co-infected with human and avian IAVs simultaneously. The main question, however, is: what is the glycome in the explants, or directly from tissues?

Overall, the manuscript is clearly written and provides new insights into the behaviour of the cattle isolate, now compared with a representative group of model or precursor HAs of different origins.

It would be great if a consistent nomenclature for the IAV strains could be used in the study. There is a mix of origin (Texas), animal from which the virus was isolated (mallard), or abbreviations that do not follow guidelines (IAV07). Are the USSR and Udorn not lab-adapted?

The experimental setup includes bovine mammary primary and continuous cells, as well as mammary explants. Some of the most significant differences, for example, in viral fitness studies and co-infection experiments, are observed in these explants. Perhaps there could be some additional focus on this observation. The implications in comparison to the results obtained in cultured cells could be described. How will the human and other HA subtype viruses fare in the explants?

Reviewer #3 (Public review):

Summary:

This excellent manuscript by Pinto, Sharp, and colleagues examines bovine tissue tropism for influenza viruses. They find that bovine flu, as well as other strains, has strong replication in mammary tissue. They also map the genetic changes to influenza that improve replication in bovine cells. Overall, the study is well designed and executed, and the results are very timely.

Strengths:

(1) The experiments are well-controlled.

(2) The figures are well-constructed and easy to follow.

(3) The Methods and legends are detailed, with sufficient information.

Weaknesses:

(1) A comparison to human cells would strengthen the overall impact of the results. Are human mammary cells also uniquely susceptible to influenza? Are bovine mammary cells special in some way?

(2) For the virus infection studies with segment 8 swaps, it should at least be noted that some of the phenotypes could be driven by NEP.

(3) The data demonstrating that bMEC can support co-infection are compelling and important, but would be strengthened with a comparison from a different cell type or species. Do mammary cells uniquely support higher co-infection?

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Here, Pinto and colleagues set out to investigate whether the cow udder is a potential mixing site for the influenza virus. The authors have demonstrated that bovine mammary epithelial cells can be infected with both avian and human influenza A viruses, supporting the idea that the cow udder may be a potential site for reassortment. Furthermore, they demonstrate that the bovine-adapted IAV replicates to similar titers in avian epithelial cells when compared to an AIV precursor virus. Thus, suggesting there is no fitness trade-off, and confirms the potential for spill-back of the cattle B3.13 into poultry, which has already been observed. Overall, I believe the authors achieved their aims. However, there are instances in which the results do not entirely support the conclusions (noted in weaknesses). Given the ongoing questions surrounding highly pathogenic avian influenza A virus in dairy cows, this work provides valuable evidence for the potential of the cow udder as a site of reassortment. These findings highlight the need for surveillance of influenza A virus incursions into livestock species, particularly cows. Some specific strengths and questions regarding weaknesses have been outlined below.

Strengths:

(1) The authors use a diverse range of cell types and influenza A virus strains, as well as a wide range of techniques to address the questions at hand.

(2) The use of cells from multiple bovine breeds for the MAC-T, bMEC and explants suggests the phenomenon is not unique to a single breed.

(3) The results suggesting there is no fitness trade-off for Cattle Texas in an avian host are interesting, and confirm the potential for spill-back of the cattle B3.13 into poultry, which has been observed.

Weaknesses:

I have listed my complete questions/concerns below. However, there are two main weaknesses of the article in its current state. Firstly, there is no apples-to-apples comparison in terms of determining a preference for IAV to infect the cow udder over other organs (Q4). The mammary gland and respiratory tract are represented by epithelial cells, but for other organs, fibroblasts were chosen. I think the fairer comparison would be to compare epithelial cells from different organs to demonstrate a preference for the mammary gland. Secondly, the main premise of the article relies on bMEC and MAC-T (primary and immortalised mammary epithelial cells), facilitating higher viral growth than the cells from other organs. Yet throughout the article, a 10x higher dose of IAV is used in the bMEC cells compared to everything else (Q6). This raises the question of how much of the results are due to a preference for the mammary epithelial cells, and how much is simply due to the increased dose.

When we set out to test if cow mammary gland cells were particularly susceptible to IAV infection compared to other bovine cell types, we used what was available in the Roslin Institute in the first instance – a mix of primary and continuous cells from various anatomical sites: three epithelial cell types (two mammary, one respiratory tract) two immune cell types and four sets of fibroblasts from various organs. Given the representation of different anatomical sites, cell types and differentiation statuses, we considered this a suitably diverse panel with which to characterise infection dynamics of a broad range of IAVs, before more focussed investigations using the mammary bMEC and explant tissues. Both mammary epithelial cell types grew our library of influenza challenge strains significantly better than the BAT-II respiratory epithelial cells, as well as the two immune cell types and all four fibroblast populations. Of the fibroblast cells, those derived from the brain grew IAV significantly better than the skin and turbinate fibroblasts, while blood-derived macrophages grew virus significantly better than the lymphocytes and non-brain fibroblasts. Therefore, there are “apple to apple” comparisons as well as apple to pear comparisons that give significant differences. We therefore think that our conclusions (in the abstract) that mammary cells are particularly replication competent for IAV, (at the end of the introduction) that “a wide range of cow-derived cells are susceptible” and that (in the results section) that “mammary cells showed the highest susceptibility” are entirely justifiable. We do not claim that mammary cells are the only permissive bovine cells, but our evidence suggests they are highly susceptible.

We used a higher MOI for bMECs because test experiments with WT PR8 and the Cattle Texas 6:2 reassortant showed that MOI 0.01 infections gave more variable results than ones run at MOI 0.1, perhaps because of the intrinsic variability of mixed primary cell populations. We therefore chose to go with the higher MOI. However, the end-point titres between the two conditions were not significantly different, so we do not think this choice is a confounding issue. We will add the comparison of the two MOIs as a supplementary figure in the formal revision.

Reviewer #2 (Public review):

The authors use a library of influenza A viruses from different strains, classified in lab-adapted, human, avian, and swine according to the animal from which they were isolated. They propose that the cow mammary gland serves as a mixing vessel for influenza A viruses. As a first approach, the authors assess susceptibility to infection across different cell types, including continuous and primary cell lines, bovine mammary cells, and mammary explants. All these cells support polymerase activity. Then, they analyzed changes in the bovine virus's viral fitness relative to an avian precursor. The authors use single-gene replacement to study whether and which RNP segments improve viral transcription. As part of this section, they also test IFN-specific antagonism by NS1 to assess the input of segment 8. Quantitative glycomic analysis was performed on the continuous bovine mammary cell line to demonstrate the presence of both a2,3 and a2,6, which is consistent with their observation that these cells can be co-infected with human and avian IAVs simultaneously. The main question, however, is: what is the glycome in the explants, or directly from tissues?

We report quantitative glycomics for the primary bovine mammary epithelial cells as well as the continuous line the referee highlights. However, we agree with R2 that a detailed glycomic analysis of primary bovine mammary tissue would allow a better understanding of the actual glycosylation status in vivo. This has now been undertaken by the authors and is available as a bioRxiv preprint:

Bovine H5N1 influenza viruses have adapted to more efficiently use receptors abundant in cattle

Jack A. Hassard, Jiayun Yang, Bernadeta Dadonaite, Jonathan E.Pekar, Jin Yu, Samuel A. S. Richardson, Rute M. Pinto, Kristel Ramirez Valdez, Philippe Lemey, Jessica L. Quantrill, JinghanXue, Tereza Masonou, Katie-Marie Case, Jila Ajeian, Maximillian N. J. Woodall, Rebecca A. Ross, Nicolas Hudson, Kan Zhong, Hongzhi Cao, Samuel Jones, Hannah J. Klim, Brian R. Wasik, Desi N. Dermawan, Jean-Remy Sadeyen, Dirk Werling, DylanYaffy, Joe James, Alessandro Nunez, Paul Digard, Ian H. Brown, Daniel H. Goldhill, Pablo R. Murcia, Claire M. Smith, Yan Liu, Jesse D. Bloom, Munir Iqbal, Wendy S. Barclay, Stuart M.Haslam, Thomas P. Peacock: bioRxiv 2026.04.02.715584; doi:https://doi.org/10.64898/2026.04.02.715584

Overall, the manuscript is clearly written and provides new insights into the behaviour of the cattle isolate, now compared with a representative group of model or precursor HAs of different origins.

It would be great if a consistent nomenclature for the IAV strains could be used in the study. There is a mix of origin (Texas), animal from which the virus was isolated (mallard), or abbreviations that do not follow guidelines (IAV07). Are the USSR and Udorn not lab-adapted?

We chose the abbreviated names for a variety of reasons. Partly from common usage (e.g. PR8, Udorn), partly for consistency with other already published papers from the FluTrailMap consortia (e.g. Cattle Texas; Dholakia et al 2026), partly to make diversity obvious in certain figures (e.g. H3N1, H5N2 etc) and partly to avoid confusion between viruses that originate from the same geographic area (e.g. AIV07, AIV09, H5N8-20 etc which are all Ck/England/isolate numbers). Overall, we found it more confusing to use the expanded nomenclature. Re AIV07 which the referee criticises for not following naming guidelines – if this is a reference to the EURL nomenclature, AIV07 is the abbreviation for the specific virus A/Chicken/England/053052/2021, our representative virus for EURL genotype EA-2020-C, as we say in the text. We should however have included this nomenclature in Table 1, which otherwise provides a cross-reference for all the names. This will be added in the formal revision to help with clarity.

As to whether USSR and Udorn are lab adapted – that depends on definitions. There is a continuum of adaptive changes and/or sequence drift starting from the very first growth of an isolate in the laboratory. The viruses we define here as lab adapted are ones that have been deliberately adapted to other hosts or which have very long passage histories in multiple host species resulting in known functionally significant changes. For example, PR8, with 100s of passages in mice, ferrets and embryonated hens eggs (doi: 10.3390/v12060590), makes it unarguably lab-adapted. We admit that A/USSR/77 and A/Udorn/307/1972 are probably further along this adaptive pathway than more recent isolates such as A/Norway/3433/2018, but are unaware of any specific reason that would put them into our lab adapted category.

The experimental setup includes bovine mammary primary and continuous cells, as well as mammary explants. Some of the most significant differences, for example, in viral fitness studies and co-infection experiments, are observed in these explants. Perhaps there could be some additional focus on this observation. The implications in comparison to the results obtained in cultured cells could be described. How will the human and other HA subtype viruses fare in the explants?

We agree that this is an important and interesting question, and have tested the strains we used for co-infections, human seasonal H1N1 “Norway” and low pathogenic avian influenza “H3N1”, in the mammary explants. Both replicate, the avian virus to 20-fold higher titres. We will add this new information to the revised manuscript.

Reviewer #3 (Public review):

Summary:

This excellent manuscript by Pinto, Sharp, and colleagues examines bovine tissue tropism for influenza viruses. They find that bovine flu, as well as other strains, has strong replication in mammary tissue. They also map the genetic changes to influenza that improve replication in bovine cells. Overall, the study is well designed and executed, and the results are very timely.

Strengths:

(1) The experiments are well-controlled.

(2) The figures are well-constructed and easy to follow.

(3) The Methods and legends are detailed, with sufficient information.

Weaknesses:

(1) A comparison to human cells would strengthen the overall impact of the results. Are human mammary cells also uniquely susceptible to influenza? Are bovine mammary cells special in some way?

This is an interesting question but we have not tested mammary gland cells from humans (or any other species of mammal), but we have reported elsewhere (Dholakia et al., Nat Commun. 2026 Jan 16;17(1):1603. doi: 10.1038/s41467-026-68306-6.) that Cattle Texas grows well in a variety of human respiratory cells. Here we are considering the bovine mammary organ as a potential reassortment site for IAVs; human mammary organs are unlikely to create this opportunity.

(2) For the virus infection studies with segment 8 swaps, it should at least be noted that some of the phenotypes could be driven by NEP.

We agree, and will change the text to acknowledge this in a revised version.

(3) The data demonstrating that bMEC can support co-infection are compelling and important, but would be strengthened with a comparison from a different cell type or species. Do mammary cells uniquely support higher co-infection?

We have data showing that co-infection also occurs in the continuous MAC-T udder cell line and will include these data in a revision. We have not tested bovine cells from other organs for co-infection potential as they do not seem to be significant sites of infection in vivo.

eLife Assessment

This potentially important paper questions the evolutionary origin of the tunicate endoderm, using single-cell sequencing on a developmental series of the ascidian Styela clava that covers metamorphosis and gut development. The authors base their conclusions on a comparison with the development of mouse gut endoderm, where they point out similarities in the origin of tissues, perhaps representing a case of "deep homology". This work has the potential to make a significant contribution to the field of chordate evolution, but in its current form, the evidence it presents is incomplete and is limited by a problematic discussion of evolutionary implications and by major issues regarding the clarity and cogency of data presentation.

Reviewer #1 (Public review):

Summary:

The authors employ state-of-the-art single-cell sequencing technologies to map the gene expression profiles of the developing digestive tract in the ascidian Styela clava, a member of the invertebrate sister group to vertebrates. This data has the potential to provide a new perspective on the relationships between the guts of an invertebrate like this ascidian relative to vertebrate systems. Key findings include the elaboration of our understanding that the Styela gut arises from two distinct cellular origins, with this being comparable to the dual embryogenic origin of vertebrate guts (at least, as exemplified by the mouse digestive tract arising from both definitive and visceral endoderm).

Strengths:

The resolution that can be achieved from the series of developmental stages analysed by the authors through the metamorphosis and early gut specification and development is vital to the strength of this new dataset. This new scRNAseq data is likely to provide a useful foundation for future work that delves into the functions of various genes within regions of the ascidian gut.

Weaknesses:

The main weakness of the manuscript as it currently stands is the lack of clarity about the genetic comparisons between ascidian and mouse, and what the precise genetic underpinnings are for any statements of similarity.

Reviewer #2 (Public review):

This manuscript explores endodermal lineage specification during metamorphosis in Styela clava. As biphasic lifestyle organisms, the endoderm exists as a rudiment in the non-feeding larvae that differentiates throughout metamorphosis to build the digestive components of the adult body plan. The authors of this manuscript use scRNA sequencing of individuals throughout the metamorphic process, as well as maturing juveniles, to follow the trajectories of the endodermal precursors. They identify two distinct populations that give rise to the stomach and intestinal lineages, and they suggest that there are homologous relationships between tunicate & vertebrate dual-origin endodermal lineages. Additionally, the authors highlight the role of conserved FGF signal-dependent programs in digestive organ patterning and suggest that endodermal fate restriction occurs earlier in Styela in comparison with the mouse gut.

Overall, the paper is the first in-depth look at tunicate endodermal fate from a single-cell sequencing perspective and provides a robust framework for understanding the evolutionary origins of the deuterostome/chordate gut. The data is substantial and of great interest. However, we find their discussion of evolutionary implications to be highly problematic, and there are also numerous major issues regarding the clarity and cogency of their data presentation. Thus, we consider that substantial revision is required to provide a more accurate analysis of this data and its evolutionary implications. This revision would not require further experimentation.

Author response:

We sincerely thank the Reviewing Editor, Senior Editor, and both reviewers for their careful and constructive assessment of our manuscript. We are encouraged that the reviewers recognize the value of our dataset and its potential contribution. We greatly appreciate the thoughtful comments and have carefully considered the reviews. We plan to revise the manuscript accordingly. 

First, we will revise and refine the cross-species comparative analysis, with particular attention to clarifying the basis of the comparisons between ascidian and mouse endodermal lineages. In particular, we will adopt a more cautious and precise comparative framework, clarify the scope and limitations of the mouse comparison, and broaden the context by incorporating additional vertebrate and invertebrate deuterostome systems where relevant.

Second, we will strengthen the gene-level interpretation of the identified endodermal populations and clarify the molecular basis for the similarities and differences. In particular, we will more clearly identify the key marker genes defining each population, better explain their relationship to previously described developmental sources. 

Third, we will improve the clarity of the Results presentation, including the description of the two major endodermal progenitor populations and their subcategories, as well as the organization of the text, figures, and figure legends. 

Fourth, we will substantially rewrite the Discussion, especially the sections dealing with evolutionary implications, to ensure that our interpretations are presented in a more cautious manner.

These revisions are intended to address the reviewers’ concerns regarding both the evolutionary framing and the presentation of the data. We believe that these revisions, which will include both rewriting and additional analyses, will improve the clarity and rigor of the manuscript. We look forward to submitting a revised version.

We thank the editors and reviewers again for their time and expertise.

eLife Assessment

This study presents a valuable finding on the role of intracellular zinc as a regulator of the sperm-specific potassium channel Slo3, demonstrating that zinc export during capacitation contributes to alkalinization-induced membrane hyperpolarization. The electrophysiological evidence supporting zinc-mediated inhibition of Slo3 is solid, though the mechanistic basis of this inhibition is not complete, as the proposed zinc-binding site involving E169 and E205 has not been directly tested through double-mutant analysis. This work will be of interest to reproductive biologists and ion channel biophysicists studying the molecular mechanisms of sperm capacitation.

Reviewer #1 (Public review):

Summary:

In their manuscript, Andriani et al. show intracellular zinc is exported from sperm during capacitation and suppresses the alkalinization-induced hyperpolarization in sperm. Intracellular zinc inhibits Slo3 current, which is enhanced by the co-expression of gamma subunit Lrrc52. Computational studies reveal that the Zn binding site on mSlo3 is located near E169 and E205, which are involved in the sustained zinc inhibition of mSlo3 current. The authors propose that intracellular zinc play a key role of sperm capacitation by inhibiting the Slo3 channel.

Strengths:

Overall, the work appears well designed (e.g., oocyte patch-clamp experiments), and clearly presented. Three-dimensional structural modeling and flooding simulations are executed.

Weaknesses:

The simple mutagenesis analysis of E169 and E205 showed partial abolishment, but the molecular mechanism by which zinc inhibits Slo3 current is not yet fully shown. The authors should consider performing more extensive experiments, such as creating double mutants or combination mutants involving other residues. Additionally, could other mechanisms explain the role of zinc in regulating the Slo3 current?

While elucidating the mechanism of Slo3 is interesting, there is substantial literature indicating how zinc regulates channel functions at a molecular level. Given this, the manuscript should provide a deeper understanding by clearly elucidating the molecular mechanism of the regulation of Slo3 current by zinc.

The manuscript includes no experimental data on the mechanism of intracellular zinc export during sperm capacitation, despite being crucial for the regulation of sperm function.

Reviewer #2 (Public review):

Summary:

In this paper, Andriani and colleagues are examining the potential role of Zn flux in sperm and its effect on Slo3 channels. This is an interesting question that is likely critical to how sperm function properly and Slo3 channels are a possible candidate for a downstream molecule that is impacted by Zn. In this paper the authors using Zn imaging, sperm motility assays, and electrophysiology to show that Zn flux has impacts on sperm function. They then go on to look at the impact Zn has on Slo3 current and propose a binding site based on MD simulations. Revisions of the paper added new critical controls and improved description of the methodology.

Strengths:

The question of how Zn flux impacts membrane potential and sperm motility is an important one. Moreover, Slo3 make present an interesting candidate or the target of Zn regulation. The combination of methods used here also has the potential to uncover mechanisms of Zn regulation of Slo3.

Weaknesses:

The responses sufficiently answered my original concerns.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their manuscript, Andriani et al. show intracellular zinc is exported from sperm during capacitation and suppresses the alkalinization-induced hyperpolarization in sperm. Intracellular zinc inhibits Slo3 current, which is enhanced by the co-expression of gamma subunit Lrrc52. Computational studies reveal that the Zn binding site on mSlo3 is located near E169 and E205, which are involved in the sustained zinc inhibition of mSlo3 current. The authors propose that intracellular zinc plays a key role in sperm capacitation by inhibiting the Slo3 channel.

Strengths:

Overall, the work appears well-designed (e.g., oocyte patch-clamp experiments), and clearly presented. Three-dimensional structural modeling and flooding simulations are executed.

Weaknesses:

The simple mutagenesis analysis of E169 and E205 showed partial abolishment, but the molecular mechanism by which zinc inhibits Slo3 current is not yet fully shown. The authors should consider performing more extensive experiments, such as creating double mutants or combination mutants involving other residues. Additionally, could other mechanisms explain the role of zinc in regulating the Slo3 current?

We thank the reviewer’s thoughtful comments regarding the mutagenesis analysis and the possible mechanisms underlying zinc regulation of Slo3. Regarding the suggestion to perform double or combination mutants, we agree that such experiments would provide valuable mechanistic insight. However, due to limited resources, we were not able to perform these additional experiments within the scope of this study. Our current results show that mutations at E169 and E205 partially abolish zinc inhibition, which suggests that the inhibitory mechanism is not mediated through a single residue and is likely more complex.

Alternative mechanisms that may contribute to zinc modulation of Slo3 include indirect effects through modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites within Slo3 channel other than the sites discovered through this study. At present, these mechanisms remain speculative and further studies will be required to clarify their contributions. This study provides the foundational basis for understanding how zinc inhibits the Slo3 channel and serves as an important starting point for defining the molecular mechanism in more detail.

We already acknowledged in the Discussion section that the precise molecular basis of zinc inhibition remains unknown and that future work involving more extensive mutational and structural analyses will be essential to fully resolve this issue.

We also added the discussion section as follows:

“It is worth noting that the incomplete loss of zinc sensitivity in these mutants suggests that additional mechanisms may participate in zinc modulation of Slo3. These may include modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites. Comparisons with Slo2.2 (J. Zhang et al., 2023), KCNQ4 (Gao et al., 2017), and voltage-gated calcium channels (Sun et al., 2007) further support the possibility of diverse molecular determinants for zinc inhibition. Our VCF, mutagenesis, and simulation data together indicate that zinc influences voltage sensor movement in mSlo3, which may suggest a distinct inhibitory mechanism that warrants further investigation.”

While elucidating the mechanism of Slo3 is interesting, there is substantial literature indicating how zinc regulates channel functions at a molecular level. Given this, the manuscript should provide a deeper understanding by clearly elucidating the molecular mechanism of the regulation of Slo3 current by zinc.

Thank you for highlighting a very important point that requires deeper discussion and explanation regarding how zinc regulates Slo3 current at the molecular level. As reported, Slo3 is gated by membrane depolarization and, at the same time, this channel is also gated by intracellular pH, particularly alkalinization (Leonetti et al., 2012; Schreiber et al., 1998; X. Zhang et al., 2006). This makes the gating mechanism of this channel complex. The molecular mechanism underlying pH regulation of the Slo3 channel remains unknown (M. D. Lyon et al., 2023). We tested different pH conditions and membrane voltage to elucidate the effect of zinc on the Slo3 channel. Our data suggests that zinc inhibition in mSlo3 channels is dependent on pH (Fig. 2A-E), voltage (Fig. 2G-H; Fig.2—figure supplement 1A, B) and exhibits a long-lasting inhibitory effect (Fig. 2I, K).

However, as much as we are aware that these data alone cannot explain the molecular mechanisms of zinc’s effect on Slo3 current, our mutagenesis experiments also did not provide a straightforward answer. The single amino acid mutations examined in this study, which contain clustered negative residues, did not significantly alter zinc-mediated current reduction compared to the wild type. As the reviewer pointed out, mutating one single amino acid may not be sufficient to fully identify other contributing residues within the predicted mSlo3 zinc-binding site. Therefore, more extensive mutagenesis studies will be required to fully elucidate the molecular mechanism of zinc inhibition in mSlo3, which could not be fully understood in this study.

On the other hand, when we analyzed the percentage of current recovery of all the mutants, E169A and E205A showed significant current recovery upon the wash-out by pH 8.0 alone. Consistent with MD simulations, our electrophysiological recordings demonstrated that the long-lasting inhibitory effect of zinc was partly abolished by these mutations. Thus, our findings highlight the contribution of E169A, located at the lower end of S3 domain and E205A, located at the lower region of S4 domain, to zinc-mediated inhibition of mSlo3 current.

Additionally, since the molecular mechanism of pH regulation on Slo3 channel remains unknown, the molecular basis of its dual gating has yet to be elucidated, making it difficult to draw a single definitive conclusion from our current research data on how zinc inhibits mSlo3 current. Nevertheless, this study provides the foundation for understanding possible mechanisms of zinc inhibition. Our VCF data suggest that zinc influences the movement of VSD of mSlo3, and together with our mutagenesis and MD simulations results, these findings represent an important first step toward elucidating the molecular mechanism of zinc inhibition of the mSlo3 current.

Intracellular zinc exerts inhibitory effect on mSlo3, similar to what has been reported for Slo2.2 channels (J. Zhang et al., 2023), high- and low-voltage activated calcium channel families (Sun et al., 2007) and KCNQ4 channels (Gao et al., 2017). These studies identified different regions, amino acids, and possible mechanisms of zinc inhibition among these ion channels. For instance, in Slo2.2 channels, which belong to the same Slo family as Slo3, the zinc-binding site was identified in the RCK2 domain, where cysteine and histidine residues form a canonical zinc binding motif (J. Zhang et al., 2023). In KCNQ4 channels, zinc inhibits the channel activity in a non-canonical manner that depends on its physiological activator, the membrane lipid PI(4,5)P₂ (Gao et al., 2017). Although zinc exerts the inhibitory effects on those various voltage-gated potassium and calcium channels, the mechanisms differ. Our data suggests another distinct mechanism of zinc inhibition in the mSlo3 channel with the identified sites located in the VSD, where zinc influences the voltage-sensor motion, and consequently affects the complex gating of Slo3.

We revised the discussion section as follows, which is also related to the previous comment:

“It is worth noting that the incomplete loss of zinc sensitivity in these mutants suggests that additional mechanisms may participate in zinc modulation of Slo3. These may include modulation of nearby charged residues, structural rearrangements influenced by zinc binding, or the presence of multiple zinc binding sites. Comparisons with Slo2.2 (J. Zhang et al., 2023), KCNQ4 (Gao et al., 2017), and voltage-gated calcium channels (Sun et al., 2007) further support the possibility of diverse molecular determinants for zinc inhibition. Our VCF, mutagenesis, and simulation data together indicate that zinc influences voltage sensor movement in mSlo3, which may suggest a distinct inhibitory mechanism that warrants further investigation.”

The manuscript includes no experimental data on the mechanism of intracellular zinc export during sperm capacitation, despite being crucial for the regulation of sperm function.

We thank the reviewers for the valuable comment in this regard. We agree that mechanism of intracellular zinc export during capacitation is crucial for the regulation of sperm function, and it would be an important finding if we could provide the experimental data on this. However, there are significant technical difficulties in performing such experiments. Two protein families facilitate the transport of zinc across cellular and intracellular membranes in opposite directions: ZnT and ZIP. ZIP12 has been reported to be highly expressed in mouse testis (Zhu et al., 2022), as well as ZnT-1 (Elgazar et al., 2005). To date, there are no known inhibitors for zinc transporters, and there is also no suitable antibodies available for these transporters, which makes it difficult to design experiments to examine the intracellular zinc transport during sperm capacitation. Apart from the two reported zinc transporters, the functional significance of other ZnTs and ZIPs, particularly those related to capacitation, remains largely unclear, leaving the mechanisms of zinc transport in sperm during capacitation poorly understood. Moreover. homozygous Znt-1 knockout mice exhibit a lethal phenotype (Andrews et al., 2004).

Reviewer #2 (Public review):

Summary:

In this paper, Andriani and colleagues are examining the potential role of Zn flux in sperm and its effect on Slo3 channels. This is an interesting question that is likely critical to how sperm function properly and Slo3 channels are a possible candidate for a downstream molecule that is impacted by Zn. In this paper, the authors use Zn imaging, sperm motility assays, and electrophysiology to show that Zn flux impacts sperm function. They then go on to look at the impact Zn has on Slo3 current and propose a binding site based on MD simulations. While the ideas are interesting, the experiments are not well described in many places making understanding the results very difficult. In addition, critical controls are missing throughout the paper.

Strengths:

The question of how Zn flux impacts membrane potential and sperm motility is an important one. Moreover, Slo3 presents an interesting candidate or the target of Zn regulation. The combination of methods used here also has the potential to uncover mechanisms of Zn regulation of Slo3.

Weaknesses:

Much of the paper lacks experimental description which makes interpretation quite difficult, or a detailed discussion is missing. Examples include:

(1) Figure 1, particularly the Zn imaging, is not sufficiently described. How is the fluorescence intensity measured? A representative ROI? The whole tail and head? Are the sperm immobile? If not, there is evidence that motion artifacts can significantly distort these sorts of measures from Calcium measurements in Cilia. Were there controls done? Is the small amount of Zn seen in the tail above the background?

We sincerely thank the reviewer for pointing out important details that we should provide in this study in order to make it well understood. We would like to answer and respond to the points raised by reviewer as follows:

Fluorescence intensity is measured by the signal taken from the whole head and the proximal part of tail in sperm. We have included this in the materials and methods.

Materials and Methods

“Fluorescence intensity is measured by the signal taken from the whole head and the proximal part of tail in sperm.”

Yes sperm is immobile during zinc imaging.

We added the control data of zinc imaging without capacitation medium and incorporated the data into the graph in Figure 1B. For the control in non-capacitation medium, we use HS medium as newly explained in the methods, results, related figure (Figure 1B), and figure legends.

Yes the small amount of Zn seen in the tail above the background. As shown in Fig. 1A we confirmed that the signal intensity at the proximal region of the tail was higher than the background. Therefore, the data for this region were calculated after background subtraction.

(2) The second half of Figure 1 is also not well described. What is the extracellular solution in the recordings? When you apply the Zn ionophore, do you expect influx or efflux? I assume efflux is based on the conclusions but this should be discussed explicitly.

The extracellular solution in the recordings for Figure 1 is HS solution (HEPES-buffered saline solution), a standard non-capacitation medium. We will include this information in the materials methods.

Materials and methods

“HS-based solution was used as the extracellular solution.”

We assume that intracellular zinc levels increase upon application of zinc ionophore. Previous work has reported that sperm contain approximately 35.7 ng/10⁶ cells in the head and flagellum (Henkel et al., 1999). When zinc pyrithione is applied, it facilitates the influx of Zn²⁺ from the surrounding medium into the cell, thereby increasing intracellular zinc concentration. Zinc pyrithione functions both as a zinc source and as a transport facilitator, allowing Zn² to cross the otherwise impermeable lipid membrane without compromising membrane integrity.

(3) Figure 2H labels the Y axis, "normalized current". Normalized to what? Why do neither of the curves end at 1? A better description of what this figure represents is needed.

Normalization for figure 2H was performed by dividing the absolute current of mSlo3 at pH 8.0 of each voltage by the absolute current at the pre-determined highest voltage that still produced a stable mSlo3 current (i.e., good patch, good clamp). In this analysis, +140 mV was chosen as the highest voltage for normalization, since in few cells the patch was lost at +160mV and +180mV. Similar to the control condition, the absolute current of mSlo3 in the presence of 100 µM zinc was normalized to the absolute current of the control at +140 mV. This information has been included in the figure legends and the Materials Methods section of the revised manuscript.

Materials Methods section:

Figure legends for figure 2H has been updated.

(4) The alpha fold simulations are not well described. How many Zn binding sites were found? Are all of the histidine mutations in Figure 4 Supplement 1 the ones that were found?

We thank the reviewer for the question. In our AlphaFold3 input, we only input the transmembrane region of the protein. From there, we found four sites located as follows:

Given that we are only interested in the intracellular side of the membrane, we are only interested in the site with the highest pLDDT value (confidence values). On the IC side, there are only two sites, where the other sites are located near the pore domain. The site is near E310 and K319.

Author response image 1.

AlphaFold3 prediction of the Zn binding site on IC side of Slo3

The histidines in Fig. 4—figure supplement 1 are all histidines that are not in the transmembrane region. These residues were not included in the initial inputs for AlphaFold3. However, we conducted MD simulations including these residues and we were able to show that a few of these residues are in contact with Zn. We have now plotted the minimum distance between each of these residues and Zn in the flooding simulations.

Author response image 2.

MD simulations of histidines residues located in IC of Slo3

Minimum distances between histidines in Fig. 4—figure supplement 1 and Zn²⁺ from the flooding simulations. Different colors indicate different repeats.

(5) There is no discussion of physiological intracellular Zn concentration. How much Zn is inside the sperm? How much if likely Free vs buffered? Is 100uM a reasonable physiological concentration?

We estimated the intracellular zinc concentration in sperm based on human sperm data, which report a zinc concentration of approximately 35.7 ng/10⁶ cells in the head and flagellum (Henkel et al., 1999). Considering the volume of a typical human sperm is about 15 µm³ (Laufer et al., 1977), this translates to an estimated intracellular zinc concentration of approximately 400 mM, although the concentration of free zinc must be much lower than this level. Although exact intracellular zinc concentrations in mouse sperm are not well-documented, this estimate supports the observation of elevated zinc in non-capacitated sperm.

There are a number of areas where the interpretation is not well supported by the data including:

(6) You say in the Figure 4 supplement, that "we did not observe any significant decrease in the percentage of current inhibition." But that is a pretty misleading statement. There are large changes (increases) in the amount of zinc inhibition. These might be allosteric changes but I don't think you can safely eliminate these as relevant Zn binding sites. Also, some of these mutations appear to allow at least some unbinding of Zn.

In our MD simulations, H720 is not at the zinc binding site and therefore, mutation to arginine would indeed eliminate its binding. We are showing this in the minimum distance analysis between Zn and H720 and show that they are further than 4 Å from each others (n=3), as shown in author response image 2.

Chimera of Slo3/Slo1 RCK2 also showed large increases in the amount of zinc inhibition, and this might serve as a potential binding site. We agree that the statement: “we did not observe any significant decrease in the percentage of current inhibition.” is misleading, therefore we revised our interpretation and statement into:

We revised the result section as follows:

“However, the percentage of current inhibition varied across the mutated constructs, showing either increases or no appreciable change (Fig. 4—figure supplement 1B, C).”

(7) Following up on the above point, it seems unfair to conclude that the D162S, E169A, and E205 mutants are part of the inhibitory binding site for Zn when the mutation has no effect on inhibition and only an effect on the washout. The mutations on the intracellular side also had an impact on the washout so it seems equally likely that they are the critical residues based on your data.

We thank the reviewer for this important point. We agree that the absence of a strong reduction in the initial zinc inhibition makes it challenging to assign any single residue as a definitive zinc binding site. However, our interpretation is based not only on the electrophysiological data but also on the MD simulations, which consistently identified E169 and E205 as residues that frequently interact with zinc and stabilize zinc occupancy within the VSD region. Although the mutations did not markedly reduce the peak level of zinc inhibition, both E169A and E205A significantly altered the long-lasting inhibitory component during washout, which is consistent with the MD-predicted interactions. In contrast, the intracellular mutations affected washout but were not supported by MD simulations as potential zinc interaction sites. Taken together, these combined datasets support the idea that E169 and E205 contribute to zinc modulation of Slo3 in the VSD, even though additional residues or mechanisms are likely involved.

(8) Nowhere in the paper do you make the specific link between Zn flux and membrane hyperpolarization via Slo3. You show that Zn flux changes the ability of the sperm to hyperpolarize and you show that Slo3 is inhibited by Zn but the connection between the two is not demonstrated. There appears to be a specific Slo3 blocker. If you use this in sperm, do you no longer see the Zn effect?

Thank you for pointing out the need for clarifying this point. It is already known that sperm capacitation is well associated with the increase of intracellular pH (Vredenburgh‐Wilberg & Parrish, 1995; Y. Zeng et al., 1996), the hyperpolarization of the membrane (Arnoult et al., 1999; Y. Zeng et al., 1995) and the elevation of intracellular Ca²⁺ concentration level (Breitbart, 2002; Publicover et al., 2007) through diverse ion channel activities. To explore whether these pathways are influenced by intracellular zinc, we used patch-clamp techniques to measure the membrane potential (Vm) as shown in Fig. 1D-K. It has been reported that under the whole-cell current clamp of mouse epididymal spermatozoa, resting membrane potential is hyperpolarized after intracellular alkalinization (Navarro et al., 2007). We mentioned this in line 100-108 in the manuscript.

Next, our findings from the experiments using mouse spermatozoa suggest that intracellular zinc inhibits a key process in sperm capacitation, specifically the alkalinization-induced hyperpolarization. Previous studies have identified the pH-and voltage-dependent potassium channel Slo3 is responsible for the principal K⁺ current (I_KSper) in mouse spermatozoa (Navarro et al., 2007; Santi et al., 2010; Schreiber et al., 1998; X. H. Zeng et al., 2011). During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010). Given this context, we next investigated whether intracellular zinc acts directly on the Slo3 channel and found that zinc inhibits mSlo3 current. We explained this rationale of the experiment in line 143-150.

We add following sentence to add more clarity to the text:

“During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010).”

Therefore, the text was modified into:

“Our findings suggest that intracellular zinc inhibits a key process in sperm capacitation, specifically the alkalinization-induced hyperpolarization. Previous studies have identified the pH-and voltage-dependent potassium channel Slo3 is responsible for the principal K⁺ current (I_KSper) in mouse spermatozoa (Navarro et al., 2007; Santi et al., 2010; Schreiber et al., 1998; X. H. Zeng et al., 2011). During capacitation, the rise in pHi leads to the activation of Slo3 channels, resulting in membrane hyperpolarization (Santi et al., 2010). Given this context, we next investigated whether intracellular zinc acts directly on the Slo3 channel.”

Regarding the specific inhibitor, as has been pointed out by the reviewer that a new Slo3 inhibitor, VU0546110, exhibited more than 40-fold selective for human Slo3 over Slo1 (M. Lyon et al., 2023). However, the effect of VU0546110 in mSlo3 has not been tested yet. Both mouse and human Slo3 exhibit similar responses to certain inhibitors, but mouse and human Slo3 is also differ in their responses to several other inhibitors (M. D. Lyon et al., 2023), making it uncertain if this VU0546110 will work on mSlo3.

(9) In the second half of Figure 1, the authors suggest that there is "no hyperpolization in 100uM Zn. That is not really true. It is reduced but not absent.

We modified the wording of “no hyperpolarization in 100 µM Zn” to “alkalinization-induced hyperpolarization was reduced in the 100 µM ZnCl₂ group.”

“In contrast, alkalinization-induced hyperpolarization was reduced in the 100 µM ZnCl₂ group”

(10) The claim that Lrcc52 with Slo3 shows a higher current inhibition at pH 7.5 than pH 8 is not well supported because there are only 3 replicates in the 7.5 case. In addition, the claim is made in the test that 100uM ZnCl2 "already inhibited mSlo3+Lrcc52 at pH7.5", contrasted with mSlo3 alone, is not tested statistically.

Thank you for the valuable comment. Although Fig. 3F shows a statistical difference, we agree that having only three replicates at pH 7.5 may somewhat weaken the conclusion. Following this suggestion, we have revised the sentence as follows:

“Alkalinization appeared to increase the percentage of current inhibition by 100 µM ZnCl₂.”

We provided statistical analysis to compare pH 7.5 between mSlo3 alone and mSlo3+Lrrc52 in the Figure 3—figure supplement 1D:

The statistical analysis showed that 100 µM zinc significantly inhibited the mSlo3 + Lrrc52 current at pH 7.5 compared to the mSlo3 current alone. We have incorporated the necessary changes into the revised manuscript and updated the figure legends accordingly.

In a number of places, better controls are needed.

(11) How specific is this effect for Zn? Mg2+, for instance, is also a divalent cation that is in the hundreds of uM range inside the cell. Does it exert the same effect? Each ion certainly has unique preferred coordination geometries, does your predicted binding with MD show what you might expect for tetrahedral coordination with Zn? Did you test other divalent cations functionally or in silicon?

To answer this question, we have tested this by building another AlphaFold3 model, with Mg²⁺ instead of Zn²⁺. We did not opt for the all-atoms MD simulations due to the cost of the simulation. Here, the model shows that Mg are all clustered at the pore domain and does not reside anywhere near the Zn²⁺ site from both MD simulations and the AF3 model.

Author response image 3.

AlphaFold3 model of Slo3 channel with Mg²⁺

The Slo3 AlphaFold model from residue M1 to L330. The colour gradient reflects the pLDDT score range from 1.73 to 95.69. Purple sticks highlighted E169, N171 and E205. In this study, we did not examine other divalent cations in our electrophysiological recordings. Exploring their effects will be an important direction for future research.

(12) For the VCF experiments, a significantly higher concentration of Zn was used (10mM). What is the reason for this? There is no discussion of how much a "puff" is. Assuming you are using the RNA injector it is probably on the order of 50nL or less. Assuming the volume of an oocyte is 1uL that would argue that the final concentration is 500uM or higher. But this is also complicated by potential local effects of high Zn at the injection site, artifacts of injecting that much metal, and the fact that a great deal of the Zn will likely be bound to other things inside the cell. Better controls are needed for this experiment.

As pointed out by the reviewer, the volume of the oocytes is estimated to be approximately 1 µL. We performed manual injections using glass needle typically used for RNA injection. However, because the injections were done manually during real-time VCF recording (as illustrated in the experimental scheme), the exact volume of the solution injected into each oocyte could not be precisely controlled. We estimated that each drop to be approximately 50 nL, resulting in a final concentration around 500 µM, as described by the reviewer.

The rationale for using relatively high concentration was to ensure that the zinc concentration inside the oocyte reached an effective level, since manual injection may sometimes deliver less than 50 nL of solution. In some cases, injections failed entirely due to the technical difficulty of the method. Because VCF recordings are already technically difficult, we aimed to ensure that zinc injection was successful in oocytes that exhibited robust fluorescence signal by injecting an excess amount of zinc that would not disrupt normal oocyte conditions. For example, 10 mM zinc was prepared in an acidic solution (pH 2.5). We verified that this acidic condition did not affect mSlo3 current by performing control injections with the acidic solution alone, since the mSlo3 current is not activated under acidic pH conditions

Author response image 4.

VCF control experimentes: vehicle injection.

Reviewer #3 (Public review):

Summary:

The study titled "Zinc is a Key Regulator of the Sperm-Specific K+ Channel (Slo3) Function" aims to investigate the role of intracellular zinc in sperm capacitation and its regulation of the sperm-specific Slo3 potassium channel. Capacitation is a crucial physiological process that enables sperm to fertilize an egg, and membrane hyperpolarization through Slo3 activation is a well-established event in this process. The authors propose that intracellular zinc dynamically decreases during capacitation and inhibits Slo3-mediated K⁺ currents, thereby playing a regulatory role in sperm function.

Strengths:

(1) Novel Contribution to Sperm Physiology.

The study provides new insights into how zinc dynamics contribute to sperm capacitation, specifically through its direct inhibition of Slo3 activity.<br /> Previous research has focused primarily on extracellular zinc's effect on sperm function; this work expands the discussion to intracellular zinc regulation, an area with limited prior investigation.

(2) Strong Electrophysiological Evidence.

The study employs inside-out patch-clamp recordings in Xenopus oocytes to demonstrate zinc's direct inhibition of Slo3 currents. The observed slow dissociation of zinc from Slo3 suggests a long-lasting regulatory effect, adding to the understanding of ion channel modulation in sperm cells.

(3) Molecular Mechanistic Insights

Using Molecular Dynamics (MD) simulations and mutagenesis, the authors identify potential zinc-binding sites within Slo3's voltage-sensing domain (VSD), particularly E169 and E205. These computational predictions are supported by electrophysiological recordings, strengthening the argument that zinc directly binds and inhibits Slo3.

(4) Physiological Relevance and Functional Implications

The study suggests that zinc inhibition of Slo3 could contribute to sperm motility regulation during capacitation.

The authors provide sperm motility assays as supporting evidence, showing that zinc chelation affects motility only after capacitation has begun, suggesting a dynamic role of intracellular zinc in the capacitation process.

Weaknesses:

While the study presents compelling electrophysiological data and molecular insights, there are several critical gaps that must be addressed before fully supporting the physiological relevance of the findings.

(1) The authors should measure the effects in sperm cells using the patch-clamp technique to directly record Slo3 currents. By normalizing Slo3 currents to cell capacitance at different intracellular zinc concentrations, the authors can quantitatively assess the extent of Slo3 inhibition by zinc and strengthen the physiological relevance of their findings.

We thank the reviewer for the valuable comments to strengthen the physiological relevance of our findings. We provided additional data of Slo3 currents measured using perforated patch-clamp recording in sperm cells in experiments with zinc pyrithione (ZnPy) before and after the addition of 10 mM NH₄Cl. Control experiments were conducted in the absence of ZnPy, in which Slo3 current were recorded before and after the application of 10 mM NH₄Cl. These data have been integrated into Figure 1L-N and Figure 1—figure supplement 1A, B.

It is worth noting that Slo3 current in this recording might contain other endogenous current, as no specific blocker was used. Nonetheless, the data showed that the Slo3 current in sperm tends to be inhibited by zinc, as shown by the plot of absolute Slo3 current after the addition of 10 mM NH₄Cl in the absence of ZnPy (control) and in the presence of 100 µM ZnPy. There was a decrease in the fold change calculated from the absolute current before and after the addition of 10 mM NH₄Cl of ZnPy treated group compared to the control group.

We also provided data with the cell capacitance as suggested; however, cell capacitance obtained from the sperm recordings showed the capacitance throughout the head and midpiece of spermatozoa. On the other hand, Slo3 channels are not expressed in the entire spermatozoa, therefore the cell capacitance acquired from these recordings does not accurately reflect the area where the Slo3 channels are localized. Although we included normalization of Slo3 currents to cell capacitance before and after ZnPy application, this normalization should be interpreted with caution for the reasons mentioned above. The corresponding figure has been included in the supplementary data Figure 1—figure supplement 1A, B.

We added sentences to the result section as follows:

“We also measured Slo3 current using perforated patch-clamp recordings in spermatozoa treated with ZnPy, before and after the addition of NH₄ Cl. Control experiments were conducted in the absence of ZnPy, in which Slo3 current were recorded before and after the application of 10 mM NH₄Cl (Fig. 1L-N; Fig. 1—figure supplement 2A, B). Slo3 current in sperm tended to be inhibited by zinc, as shown by the plot of absolute Slo3 current after the addition of 10 mM NH₄Cl in the absence of ZnPy (control) and in the presence of 100 µM ZnPy (Fig. 1L, M). There was a decrease in the fold change calculated from the absolute current before and after the addition of 10 mM NH₄Cl of ZnPy treated group compared to the control group (Fig. 1N). Taken together, these results confirmed that intracellular zinc indeed inhibits alkalinization-induced hyperpolarization in mouse sperm.”

(2) Lack of Controls in Non-Capacitated Sperm

The claim that zinc is exported from sperm during capacitation needs stronger experimental validation.

The authors did not include a control group of non-capacitated sperm in key fluorescence imaging experiments, making it difficult to confirm that the observed zinc decrease is capacitation-specific rather than a general zinc redistribution process.

To strengthen this conclusion, experiments should be performed in non-capacitating conditions to determine whether intracellular zinc levels remain unchanged.

We added the control group of non-capacitated sperm in key fluorescence imaging experiments, as integrated in Figure 1B.

The following changes in the Results and Figure Legend sections are revised and added:

“We observed that there was a gradual and significant decrease in fluorescence intensity in both regions (Fig. 1B), particularly prominent in the flagellum (Fig. 1C). This decline suggests the active release of intracellular zinc from sperm flagellum occurs during capacitation. In contrast, the fluorescence intensity of the control group of non-capacitated sperm remained unchanged (Fig. 1B).”

Figure Legend 1B was modified accordingly.

(3) Unclear Role of Zinc in Physiological Capacitation

The study clearly demonstrates zinc inhibition of Slo3 but does not sufficiently establish how this affects capacitation at a functional level.

Additional motility and capacitation markers should be analyzed to confirm that zinc influences sperm behavior beyond Slo3 inhibition.

We thank the reviewer for this valuable comment. We fully agree that zinc can influence sperm physiology through multiple mechanisms and that its overall effects on capacitation are complex. However, the main goal of our study is to investigate the mechanism and to determine whether intracellular Zn²⁺ directly inhibits Slo3. Our results from both the heterologous expression system and the sperm membrane potential recordings consistently support this conclusion.

For these reasons, we believe that adding such assays would not clarify the role of Slo3 in capacitation but rather risk confounding interpretation. Instead, we have expanded the Discussion to explicitly acknowledge these limitations and to emphasize that future studies combining genetic or pharmacological modulation of Slo3 with comprehensive capacitation analyses will be required to fully define its physiological impact.

We added sentences to the discussion section in the revised manuscript as follows:

“Although these results support a mechanistic link between zinc and Slo3 activity, future studies that combine genetic or pharmacological modulation of Slo3 with comprehensive capacitation analyses will be required to define its physiological impact in more detail. Within this context, this study highlights the potential importance of intracellular zinc in the regulation of sperm capacitation.”

(4) Insufficient Data on Zinc-Slo3 Specificity

The authors should consider using quinidine, a known washable Slo3 inhibitor, to confirm that zinc acts specifically on Slo3 channels rather than other endogenous ion channels.

The study would benefit from including washout controls in the inside-out patch-clamp recordings, as seen in Figure 3-Supplement 1, to confirm that zinc inhibition is reversible or long-lasting.

We thank the reviewer for raising the point regarding the need to confirm that the current observed in our recordings indeed represents Slo3 current by using a specific blocker such as quinidine, as there is a possibility that endogenous currents might also be present and that zinc could act on those endogenous currents. Performing experiments with quinidine would indeed be crucial to demonstrate the specificity of Slo3 current in our patch-clamp recordings.

However, in our current experimental protocol, we apply ramp pulses multiple times and require a long series of recordings within a single session in one patch as described in the materials and methods as well as Figure 2I, Figure 4—figure supplement 1C, Figure 5B (pH 8.0 → 100 µM zinc → pH 8.0, to observe the washout effect). Incorporating quinidine into this sequence would make the protocol even longer (pH 8.0 → quinidine → washout → pH 8.0 → 100 µM zinc), which increases the likelihood of patch loss before completing the full set.

Furthermore, we have ensured that the recorded current corresponds to Slo3 by using appropriate experimental conditions, specifically the suitable voltage range for activation, a high intracellular pH (pH 8.0), and high-potassium solutions in our recordings.

(5) Missing Discussion of Zinc's Role in CatSper Regulation

The study focuses solely on Slo3 but does not mention CatSper, the principal Ca²⁺ channel essential for sperm capacitation.

Zinc has been reported to inhibit CatSper activity, which could significantly impact sperm function.

The discussion should address whether zinc's effect on Slo3 represents a broader regulatory mechanism influencing multiple ion channels during capacitation.

Thank you for the comment. To the best of our knowledge, there have been no reports showing that CatSper activity is directly regulated by zinc ions.

Furthermore, in our patch-clamp recordings with NH₄Cl and ZnPy, we observed that the normal CatSper current increased even in the presence of ZnPy, which makes it challenging to conclude whether zinc directly affects CatSper channel activity.

We added sentences to the discussion section in the revised manuscript as follows:

“In addition to that, to date, there are only few reports on the effect of zinc on other sperm ion channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper, a sperm-specific Ca²⁺ channel, in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, although this study does not provide direct evidence for zinc acting directly on CatSper (Jeschke et al., 2021).”

Final Assessment

This work presents important findings on zinc regulation of Slo3 channels, supported by strong electrophysiological and molecular analyses. However, the physiological relevance of these findings remains unclear due to missing controls, and needs additional functional assays. Addressing these issues would significantly enhance the manuscript's scientific rigor and impact.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Most of the specific comments and suggestions are in the public review. Minor additional comments primarily focused on presentation and textual errors are here.

(1) There is something strange happening in Figure 6D in the -100ish range. I think it's likely related to the reversal potential of K+.

Thank you for pointing it out. Yes in figure 6D there was strange plot in the range of -100 mV. As the reviewer has pointed out we also think that it is related to the reversal potential of potassium ions.

(2) There are a number of errors in the text that make following it difficult. For instance, multiple times the authors say "In consistent" (line 120 as an example) when I think they mean consistent with.

We changed the “in consistent” with “consistent with” throughout the revised manuscript.

Reviewer #3 (Recommendations for the authors):

The authors provide well-described experiments, particularly those examining the effects of intracellular zinc on Slo3 channels using inside-out patch-clamp recordings. However, some experimental designs intended to assess the physiological relevance of these findings during capacitation require additional controls and data before the authors' claims can be fully supported.

Comments

Major Concerns & Suggested Improvements

Line 65: "In the present study, we find that intracellular zinc is exported during capacitation, indicating that zinc dynamics in spermatozoa play an important role in fertilization."

This claim requires additional experimental data to be fully supported.

Thank you for pointing it out. We have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Line 79: "Intracellular zinc is exported from sperm during capacitation."

The authors should include controls in non-capacitated conditions to determine whether zinc export is specific to capacitation or a general process in sperm cells.

Again, we have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Figures - General Comment:

In all figures, please replace SEM (Standard Error of the Mean) with Standard Deviation (SD) for consistency and a more accurate representation of variability.

SEM (Standard Error of the Mean) has been replaced with SD (Standard Deviation) in all figures (main figures and supplements) as well as in numerical description accordingly.

Figure 1

Panel B:

Include a non-capacitating media control to confirm that the observed decrease in zinc-sensitive dye fluorescence is not due to artifact/photobleaching.

We have provided data for control experiments of zinc imaging in non-capacitated conditions in Figure 1B.

Perform an experiment with capacitating media supplemented with a higher concentration of zinc. If intracellular zinc export is a real effect, added extracellular zinc should prevent or reduce this phenomenon.

We appreciate the reviewer’s suggestion; however, we believe that supplementing the medium with high concentrations of zinc is unsuitable for validating the export phenomenon due to confounding physiological factors. Our preliminary tests demonstrated that increasing extracellular zinc triggers a drastic increase in intracellular zinc as well (Author response image 5). Furthermore, the high concentration of BSA in the capacitation medium acts as a potent zinc buffer, precluding precise control over free Zn²⁺ levels. Therefore, the inherent difficulty in maintaining defined extracellular and intracellular Zn²⁺ gradients makes the interpretation of such data highly problematic. Future studies will focus on identifying the specific zinc transporters involved and characterizing their molecular mechanisms.

Author response image 5.

Zinc addition

Clarify whether the "n" value represents different cells or multiple recordings from the same cell.

n value represents different cells.

Supplemental Figure 1:

Incorporate Δ (delta) comparison between 10 min and 2 hours under control conditions and in the presence of TPEN.

Here we provide data:

Author response image 6.

Δ comparition between control and TPEN

Provide statistical analysis for these comparisons to make the effects of capacitation clearer.

We did the calculation and statistical analysis, however there was no statistical difference, as shown in the author response figure 6 due to high variability of individual data.

Figure 2

Panel C:

Incorporate inhibition at pH 7.4 and 6.0 for direct comparison.

Recording inhibition effect of zinc at pH 6.0 is not possible because there would be no current to begin with, as mSlo3 is gated by both voltage and alkaline pH.

Panel D:

Include a washout control, similar to what is shown in Panel A.

We included a washout control trace to Figure 2D.

Panel E:

Provide a longer reference trace in the absence of zinc to clearly visualize the control condition. The current reference segment is too short to properly assess baseline activity.

Although we do not have a longer reference trace in the absence of zinc for Figure 2E, we instead show the trace recorded under the application of 0.1 µM zinc in Figure 2—figure supplement 1A to illustrate the current behavior.

Panels G-H:

Include inside-out patch-clamp traces and quantification of zinc washout effects.

Inside out patch traces are shown in Figure 2G as we applied step-pulses protocol. The zinc washout effect could not be quantified because the patch was usually lost after the second step-pulse application.

Panels I-K:

Provide additional traces. In Panel I, the inhibition by zinc is clear, but in Panel J, the reduction appears less distinct and could be due to rundown or an artifact. Additional controls should clarify this.

Figure 2K presents the most representative trace among five recorded cells. The apparent reduction is less distinct, likely due to an artifact caused by a bubble in the rapid perfusion system during solution exchange. However, at the end of zinc application (t = 50 s), the current amplitude was clearly reduced compared with that at t = 0–10 s.

Figure 3

Panel D:

Include additional data showing the transition to pH 6 and washout with pH 7.5, similar to the experimental design in Panels A and B.

We included additional data showing raw trace of the application of pH 6.0 in Figure 3D, also included the transition to pH 6 and washout with pH 7.5 in Figure 3E.

Figure 3-Supplement 1:

Include zinc washout experiments. This approach is one of the best ways to evaluate the reversibility of zinc inhibition on the channel.

As mentioned above, in this recording we recorded step pulses up to +180 mV. The zinc washout effect could not be quantified because the patch was usually lost after the second step-pulse application.

Figure 6

Zinc Inhibition Specificity:

The authors should use quinidine, a known washable Slo3 inhibitor, to assess Slo3 activity before and after zinc injection.

This experiment would confirm that zinc specifically inhibits Slo3, rather than affecting other endogenous channels.

We sincerely thank the reviewer for this valuable suggestion. However, given the technical difficulty of these experiments, which involve lengthy VCF recordings and manual zinc injections that significantly compromise oocyte health, it is not feasible to apply quinidine at this stage.

Moreover, we observed voltage-dependent fluorescence changes around the VSD, and this change was influenced by the application of zinc, confirming that zinc specifically inhibits Slo3 rather than affecting other endogenous channels.

Discussion - Key Revisions Needed

Line 308: "Our results demonstrated that intracellular zinc is exported from spermatozoa during capacitation."

This claim needs to be supported by experiments using non-capacitated conditions.

Additionally, measuring maximum and minimum zinc concentrations under different conditions would improve the interpretation of fluorescence intensity changes.

We now include negative control in non-capacitated sperm. The data is incorporated into Figure 1B.

Line 309: "We further discovered that intracellular zinc regulates alkalinization-induced hyperpolarization in mice spermatozoa, mediated by Slo3 channel."

Additional controls are needed to substantiate this claim.

At this stage of the study, we do not have access to Slo3 knockout (KO) mice; therefore, performing additional experiments is not feasible.

Line 316: "Using FluoZin3-AM for zinc imaging, we confirmed the presence of intracellular zinc in sperm (Fig. 1A), which is consistent with previous findings (Henkel et al., 1999). Our observations revealed that treatment with capacitation medium induced a decrease in zinc fluorescence intensity (Fig. 1B, C), suggesting that zinc levels are dynamic during capacitation."

This statement must be supported by negative controls, including non-capacitated sperm conditions.

We now include negative control in non-capacitated sperm. The data is incorporated into Figure 1B.

Line 327: "We also observed that zinc chelator significantly affected the sperm motility only after, but not before, capacitation (Fig. 1-figure supplement 1)."

Data presentation should be revised to highlight the effects of capacitation itself.

The discussion should specify which motility parameters were affected and why others were not.

In the text we mentioned that:

“We incubated the isolated spermatozoa with cell permeable Zn²⁺ chelator N,N,N',N'-Tetrakis(2-pyridylmethyl)ethylenediamine (TPEN) and measured the motility parameters before and after capacitation. We found that VAP (average path velocity), VCL (curvilinear velocity), and VSL (straight-line velocity) were influenced by the TPEN treatment only after the capacitation, as shown in Fig. 1—figure supplement 1. These results demonstrate that the dynamics of zinc levels during capacitation potentially contributes to sperm motility, highlighting the importance of zinc action in sperm physiology.”

Indeed, we observed that zinc chelator significantly affected the sperm motility specifically in VAP (average path velocity), VCL (curvilinear velocity), and VSL (straight-line velocity) only after, but not before, capacitation (Fig. 1—figure supplement 1). Of note, it has been recently reported that all these motility parameters (VAP, VCL, and VSL) are reduced by Slo3-specific inhibitors in human sperm (M. Lyon et al., 2023). These findings are consistent with the idea that endogenous zinc dynamics control sperm motility through Slo3 during the capacitation process.

Figure legend is revised accordingly.

Line 369: "Structural determinants of zinc inhibition in the mSlo3 channel."

The authors should include an analysis of the evolutionary conservation of the mutated sites across Slo1, Slo2, and Slo3.

If Slo3 has a unique regulatory mechanism, these sites should show high sequence variability compared to other Slo channels.

If these sites are highly conserved, the authors should explain how Slo3 differs functionally from Slo1 and Slo2 despite this conservation.

We thank the reviewer for the valuable suggestions regarding the inclusion of additional discussion points on the structural determinants of zinc inhibition in the mSlo3 channel. We performed sequence alignment by using ClustalO between mSlo3, mSlo1, and mSlo2.2. It is worth noting that only human and frog variants of Slo2.1 sequence are available in the database, so we included only Slo2.2 subtype, as our focus was on Slo3 in mouse sperm.

Based on the alignment, E169 (mSlo3 numbering) is conserved among the Slo family channels in mice, while in contrast E205 (mSlo3 numbering) is not. To date, there have been no report examining the corresponding residues to E169 (E191 in mslo1 or E176 in mslo2.2) for their zinc sensitivity. This might be because in both channels the zinc-binding sites are well defined where they are located in RCK1 domain for Slo1 (Hou et al., 2010) and RCK2 domain for Slo2.2 (J. Zhang et al., 2023). The identified binding site in Slo2.2 is conserved in Slo2.1 but not present in Slo1 and Slo3 (J. Zhang et al., 2023), further suggesting that zinc regulation differs among Slo family members. However, this does not rule out the possibility that regions surrounding E191 or E176 could provide to additional insights into zinc regulation in these channels, which could be of interest for future studies.

Interestingly, in contrast to E169, E205 is not conserved across the Slo family, making this residue unique to the mouse Slo3 channel and potentially a determinant of zinc sensitivity in mSlo3. Given that E205 is located in the S4 domain and supported by our VCF results showing that zinc inhibition influences the motion of voltage-sensing domain of mSlo3, E205 represents an important residue to be explored in future studies. Furthermore, as this residue is unique only to Slo3, it highlights the distinct functional properties of Slo3 such as its gating mechanism as it is regulated by both membrane voltage and alkalinization, which has a different voltage range of activation compared to mSlo1 (Li et al., 2024) and involves distinct ligands and gating mechanisms compared to Slo2 (J. Zhang et al., 2023).

We add the sequence alignment results into Figure 5—figure supplement 1F.

We revised the results section as follows:

“Additionally, we performed sequence alignment by using ClustalO between mSlo3, mSlo1, and mSlo2.2. It is worth noting that only human and frog variants of Slo2.1 sequence are available in the database, so we included only Slo2.2 subtype, as our focus was on Slo3 in mouse sperm. Based on the alignment, E169 (mSlo3 numbering) is conserved among the Slo family channels in mice, while in contrast E205 (mSlo3 numbering) is not. (Figure 5—figure supplement 1F).”

We revised the discussion section as follows:

“Based on sequence alignment, E169 (mSlo3 numbering) is conserved among Slo family channels in mice, whereas E205 (mSlo3 numbering) is not (Fig. 5—figure supplement 1F). To date, no studies have examined the corresponding residues to E169 (E191 in mSlo1 or E176 in mSlo2.2) for their potential zinc sensitivity, likely because the established zinc binding sites in these channels are located in the RCK1 domain for Slo1 (Hou et al., 2010) and the RCK2 domain for Slo2.2 (J. Zhang et al., 2023). The identified zinc binding site in Slo2.2 is conserved in Slo2.1 but is absent in both Slo1 and Slo3 (J. Zhang et al., 2023), further suggesting that zinc regulation differs among Slo family members. Although regions surrounding E191 or E176 may still provide additional insights into zinc regulation and could be of interest for future investigation, E205 stands out because, unlike E169, it is not conserved across the Slo family, making it unique to mSlo3 and potentially a specific determinant of zinc sensitivity in this channel.”

Figure legend is revised accordingly.

Line 392: "Physiological relevance of zinc inhibition of the mSlo3 channel in mouse sperm."

The authors should mention the effects of zinc on CatSper channels, as CatSper is also crucial for capacitation.

Slo3 inhibition may represent only one component of zinc's broader regulatory role during capacitation.

We thank the reviewer for raising this important point regarding the physiological relevance of zinc inhibition of the mSlo3 channel in mouse sperm. We agree that we should have also discussed the effect of zinc on CatSper channels, as this channel is crucial for capacitation. To date, there are only few reports on the effect of zinc on CatSper channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, which facilitating sperm to escape into female genital tract (Jeschke et al., 2021). Taking this into consideration, as the reviewer pointed out, zinc inhibition on Slo3 may represent only one component of zinc’s broader regulatory role during capacitation.

We added a sentence to the discussion section in the revised manuscript as follows:

“In addition to that, to date, there are only few reports on the effect of zinc on other sperm ion channels, and none have been reported in mouse sperm. One important study was reported by (Jeschke et al., 2021), in which seminal zinc was found to inhibit prostaglandin-induced activation of CatSper, a sperm-specific Ca²⁺ channel, in human sperm. The complex opposing action of seminal zinc and prostaglandins on CatSper may help preventing premature activation of CatSper in the ejaculate and act as a dilution sensor, although this study does not provide direct evidence for zinc acting directly on CatSper (Jeschke et al., 2021).”

The study presents valuable insights into the role of intracellular zinc in sperm capacitation and Slo3 channel function. However, the physiological impact of these findings remains unclear due to insufficient controls and missing key experimental data. The suggested revisions would strengthen the validity of the claims made by the authors and improve the overall scientific rigor of the manuscript.

Key Areas for Improvement:

Control experiments in non-capacitated conditions.

Increased statistical rigor in figure analyses.

More detailed experiments to confirm specificity of zinc action on Slo3.

Expanded discussion of zinc's role beyond Slo3, including CatSper regulation.

The authors should measure these effects in sperm cells using the patch-clamp technique to directly record Slo3 currents. By normalizing Slo3 currents to cell capacitance at different intracellular zinc concentrations, the authors can quantitatively assess the extent of Slo3 inhibition by zinc and strengthen the physiological relevance of their findings.

By addressing these concerns, the manuscript will provide a more robust foundation for understanding zinc's regulatory role in sperm physiology and capacitation.

eLife Assessment

The study presents valuable findings of an optimized E. coli cell-free protein synthesis (eCFPS) system that has been simplified by reducing the number of core components from 35 to 7; furthermore, the findings communicate a simplified 'fast lysate' preparation that eliminates the need for traditional runoff and dialysis steps. It is interesting that the system's robustness is exhibited by its applicability to nanoluc, a protein that expresses readily in many systems, to more challenging proteins like the functional self-assembling vimentin and the active restriction endonuclease Bsal. Despite the study representing an advancement towards simplifying protein expression workflows, the evidence supporting some of the claims remains incomplete: performance or efficiency claims of the new system needs to be supported by comparisons with typical cell free expression systems. Despite this shortcoming, the paper remains of interest to scientists in cell and molecular biology, microbiology, biotechnology and protein synthesis.

Reviewer #1 (Public review):

Summary:

The authors presented a simplified E. coli cell-free protein synthesis (eCFPS) system reduces core reaction components from 35 to 7, improving protein expression levels. They also presented a "fast lysate" protocol that simplifies extract preparation, enhancing accessibility and robustness for diverse applications.

Strengths:

The authors present a valuable new protocol for eCFPS, which simplifies its application.

Weaknesses:

The authors provide data for optimization but offer insufficient explanation of the fundamental mechanisms underlying the phenomenon.

Comments on revisions:

The authors have adequately addressed the concerns raised by the reviewers. However, the data added by the authors on this revision raised new concerns.

On page 17, lines 358-363, and Figure 3G, the authors compared the nLuc production of mRNA-based and DNA-based reactions using initial and optimized lysates.

The authors concluded that the optimized system showed significant enhanced transcription, which compensated for the decrease in translational efficiency. If this interpretation is correct, the low yield of the initial system is simply due to the insufficient level of effective T7 RNA polymerase in the initial lysate. Supplementing the initial lysate with sufficient T7 RNA polymerase could potentially make it outperform the optimized system, and the optimized system is not so much superior to the initial system in the protein production performance. This could be easily verified by quantifying mRNA using the real-time PCR method in both the initial and optimized systems.

Reviewer #2 (Public review):

Summary:

The authors have made a convincing argument that the current system of in vitro translation using E. coli extracts can be significantly optimized to work with much lesser components, while maintaining activity. They have showcased their improved activity using not only physical but also functional readouts.

Strengths:

The experiments are designed in a very logical and easy to understand manner, which makes it easier not only to follow the paper, but also reproduce the results. Functional assays with the synthesized proteins are a good way to demonstrate functionality and applicability of the system.

Weaknesses:

The production of the lysate requires special instrumentation, limiting accessibility.

Comments on revisions:

Thank you, authors, for addressing the minor concerns outlined in my comments. I have no further recommendations.

Reviewer #3 (Public review):

Summary:

The authors aimed to overcome the challenges associated with complex, conventional prokaryotic cell-free protein synthesis (CFPS) systems, which require up to thirty-five components, by developing a streamlined and efficient E. coli CFPS platform to encourage broader adoption. The main objective was to reduce the number of reaction components from thirty-five to seven, while also developing an accessible 'fast lysate' preparation protocol that eliminates time-consuming runoff and dialysis steps. The authors also sought to demonstrate the robustness and translational quality of this streamlined system by efficiently synthesising challenging functional proteins, including the cytotoxic restriction endonuclease BsaI and the self-assembling intermediate filament protein vimentin.

Strengths:

This study presents several key strengths of the optimised E. coli cell-free protein synthesis system in terms of its design, performance and accessibility.

- The reaction mixture has been dramatically simplified, with the number of essential core components successfully reduced from up to thirty-five in conventional systems to just seven.<br /> - The "fast lysate" protocol is a significant advance in terms of procedure.<br /> - The system's ability to synthesise challenging, functional proteins is evidence of its robustness.

Weaknesses:

(1) Title: "A simplified and highly efficient cell-free protein synthesis system for prokaryotes".<br /> - This title is misleading since one would expect a simplified and highly efficient cell-free protein synthesis system to yield similar protein levels compared to current cell-free protein synthesis systems. What this study shows is that the composition of cell-free protein synthesis systems can be simplified while maintaining a certain level of protein synthesis. Here, optimisation does not involve maintaining protein synthesis yield while simplifying the cell-free protein synthesis system; rather, it involves developing a simplified cell-free protein synthesis system. As mentioned in my comments below, this study lacks a comparison of protein levels with a typical cell-free protein synthesis system.<br /> - What do the authors mean by "highly efficient"? Highly efficient compared to what experimental conditions? If one is interested by the yield of protein synthesis, is this simplified system highly efficient compared to current systems?

(2) Figure 1, 3-5 :<br /> - What do relative luciferase units represent? How are these units calculated?<br /> - In this system, the level of expression depends mainly on the level of NLuc transcripts and the efficiency of NLuc translation. How did the authors ensure that the chemical composition of the different eCFPS buffers only affected protein translation and not transcript levels? In other words, are luciferase units solely an indicator of protein synthesis efficiency, or do they also depend on transcription efficiency, which could vary depending on the experimental conditions?<br /> - How long were the eCFPS reactions allowed to proceed before performing the luciferase activity measurement? Depending on the reaction time, the absence or presence of certain compounds may or may not impact NLuc expression. For example, it can be assumed that tRNA does not significantly affect NLuc levels over a short period of time, and that endogenous tRNA in the lysate is present at sufficient concentrations. However, over a longer period of time, the addition of tRNA could essential to achieve optimal NLuc levels.<br /> - The authors show that tRNA and amino acids are not strictly essential for the expression of NLuc, likely due to residual amounts within the cell lysate. However, are the protein levels achieved without added amino acids and tRNA sufficient for biochemical assays that require a certain amount of protein? It is important to note that the focus here is on optimising the simplicity of the buffer rather than the level of protein expression. In fact, the simplicity of the buffer is prioritised over the amount of protein produced. This should be made clear.<br /> - How would the NLuc level compare if all the components were optimised individually and present in an optimised buffer, compared to a buffer optimised for simplicity as described by the authors?

(3) Line 71, Streamlining eCFPS: removal of dispensable components. This title is misleading because it creates the false impression that proteins can be produced in vitro without the addition of certain compounds. While this is true, the level of protein produced may not be sufficient for subsequent biochemical analyses. This should be made clear.

(4) Figure 2: In the legend, change "(A) Protein expression levels of the eCFPS system measured at varying concentrations of KGlu and MgGlu2" to "(A) Protein expression levels of the eCFPS system using an Nanoluciferase (NLuc) reporter DNA measured at varying concentrations of KGlu and MgGlu2".

(5) Lanes 302-303: "The thorough optimization of the seven core components was a critical step in achieving high protein expression levels". What are "high expression levels"? Compared to what?

Comments on revisions:

The authors have adequately addressed the issues I had raised in my initial review.

Author response:

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

eLife Assessment

The study presents valuable findings of an optimized E. coli cell-free protein synthesis (eCFPS) system that has been simplified by reducing the number of core components from 35 to 7; furthermore, the findings communicate a simplified 'fast lysate' preparation that eliminates the need for traditional runoff and dialysis steps. This study is an advance towards simplifying protein expression workflows, and the evidence provided is solid, starting with nanoluc, a protein that expresses readily in many systems, to applications to more challenging proteins like the functional self-assembling vimentin and the active restriction endonuclease Bsal. Data on the underlying mechanisms and efficiency of the presented system in terms of protein yield relative to other known cell-free systems would greatly enhance the findings' significance and the strength of the evidence. The paper remains of interest to scientists in microbiology, biotechnology and protein synthesis.

We thank the editors for the positive assessment of our optimized E. coli cellfree protein synthesis (eCFPS) system and the "fast lysate" preparation.

As suggested, we have significantly strengthened the evidence by adding:

(1) Mechanism data: We have integrated a detailed analysis of the endogenous metabolic pathways (amino acids and nucleotides) into the Discussion section, supported by literature (Prinz et al. 1997; Yokoyama et al. 2010; Kigawa et al. 1999).

(2) Efficiency comparisons: We have added quantitative comparisons of absolute protein yields between our simplified 7-component system and the conventional 35-component system (now in Figure S3 E-F), demonstrating that our system matches or exceeds traditional titers.

Public Reviews:

Reviewer #1 (Public review):

The authors only provided the data for optimization, leaving the underlying mechanism that explains the phenomena unexplained.

We appreciate this feedback. To address the mechanism of how protein synthesis persists without exogenous additives, we have expanded the Discussion to explain how the "fast lysate" retains active endogenous enzymes. By omitting runoff and dialysis, our system preserves the metabolic capacity to synthesize amino acids (e.g., Cys and Trp from Ser) and nucleotides from residual precursors, as supported by the literature (Prinz et al. 1997; Yokoyama et al. 2010; Kigawa et al. 1999).

Reviewer #2 (Public review):

The production of the lysate requires special instrumentation, limiting accessibility. While the strengths of the study are well-emphasized, the limitations are not mentioned.

We thank the reviewer for this point. While a high-pressure homogenizer is common in many molecular biology labs, we acknowledge it may be a barrier for some. We have now included a dedicated Limitations paragraph in the Discussion addressing accessibility and the inherent challenges of prokaryotic systems in producing complex human proteins requiring post-translational modifications.

Reviewer #3 (Public review):

(1) Clarification on "highly efficient" and the lack of comparison with typical high-yield systems.

We have clarified "highly efficient" as a holistic balance of high yield, robustness, and simplified preparation. Crucially, we added absolute yield data (sfGFP standard curve) to Figure S3E-F demonstrating that our 7-component system performs comparably to or better than traditional high-yield protocols.

(2) How did the authors ensure chemical composition only affected translation and not transcription?

This is a key distinction. We performed new experiments using pretranscribed mRNA templates (Figure S3G) to isolate translational effects. While translation efficiency slightly decreased in the simplified buffer, the overall protein yield increased significantly due to a dramatic boost in transcription efficiency, confirming the system's net performance gain.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

There are specific concerns that need to be addressed:

(1) On page 4, lines 103-109, the authors speculate that protein synthesis persists even in the absence of amino acids like arginine, cysteine, and tryptophan. They suggest that this is likely due to residual amounts of these amino acids present in the cell lysate. Yokoyama et al. demonstrated that these amino acids are generated from other amino acids by endogenous amino acid metabolic enzymes in the cell lysate (J. Biomol. NMR 48, 193, (2010), doi: 10.1007/s10858-010-9455-3.). Cysteine and tryptophan can be derived from serine. In this context, asparagine and glutamine can be disregarded because they are synthesized from aspartate and glutamate, respectively. A more indepth analysis is required to interpret the results accurately.

We thank the reviewer for this insightful comment and for pointing us toward the relevant literature. We agree that the persistence of protein synthesis in the absence of exogenous amino acids like Arg, Cys, and Trp is driven by the robust metabolic capacity of our "fast lysate."

Unlike conventional protocols, our "fast lysate" procedure deliberately omits runoff and dialysis steps, ensuring the maximal retention of active endogenous metabolic enzymes and residual small-molecule pools. As demonstrated by Yokoyama et al. (2010), E. coli cell extracts retain functional enzymes capable of synthesizing acid-sensitive amino acids from precursors or more stable amino acids. We have integrated a detailed mechanistic analysis of these endogenous metabolic pathways into the Discussion section and have cited Yokoyama et al. (2010) to support this interpretation.

(2) On page 4, lines 111-115, the authors demonstrated that protein synthesis could occur even in the absence of CTP or UTP, provided ATP and GTP are present. This phenomenon can also be attributed to the analogous complementary actions of metabolic pathways.

We agree with the reviewer's assessment. The ability of the optimized eCFPS to function without exogenous CTP/UTP relies on the same principle of endogenous metabolic conversion mentioned above. The omission of dialysis ensures that the lysate retains not only residual nucleotide pools but also the full suite of nucleotide metabolic enzymes. Powered by our optimized energy regeneration system, these enzymes maintain sufficient levels of CTP and UTP to support transcription and translation. This explanation has been added to the Discussion section to clarify the robustness of our system.

(3) On Figure 3A, protein synthesis kinetics are presented in a stair plot instead of the commonly used scatterplot. Is there a specific reason for choosing the stair plot?

We chose the stair plot representation to more clearly visualize the cumulative process of protein synthesis and its stabilization over discrete time intervals. Given that sampling occurred every 10 minutes, a stair plot effectively highlights the "plateau" phases and the incremental nature of accumulation, which can sometimes be obscured by dense scatter plots.

(4) On Figure 3C. It is unclear which system is referred to as the "initial" system in Figure 3C. Which data point on Figures 3A and 3B corresponds to this "initial" system?

We apologize for the lack of clarity. In Figure 3C, "initial" refers to the traditional 35-component system prior to our streamlining process. Figures 3A and 3B characterize the performance of the final optimized system alone. To resolve this ambiguity, we have updated the legend for Figure 3 to explicitly define the "initial" system as the pre-optimization control.

(5) In Figure 5D, previously reported eCFPS and the system using "fast lysate" were compared. The only difference between the two systems seems to be the type of lysate used, according to the Supplementary table. Optimal concentrations for the components are the same for both lysates, or is there still room for optimization for "fast lysate"?

The "fast lysate" primarily differs from conventional lysates in its preparation speed and the retention of endogenous cofactors/enzymes. While the optimal salt and energy concentrations remained consistent across both lysates in our tests, the "fast lysate" provides a higher baseline signal due to the endogenous T7 RNA polymerase and metabolic factors. We believe this demonstrates the robustness of the optimized reaction buffer across varying lysate preparation qualities.

(6) The study suggests that the removal of DTT didn't negatively affect protein expression. However, based on my experience, certain proteins, especially those with cysteine residues on their surface, tend to aggregate without DTT. Did the authors attempt to express such proteins, or did they draw this conclusion based on the limited number of proteins tested?

This is a valid concern. We based our conclusion on the functional expression of Bsal and vimentin—two proteins that are inherently prone to aggregation and misfolding. Their successful synthesis suggests that the intrinsic reducing capacity of the lysate (e.g., glutathione and thioredoxin systems) is sufficient for many targets (Prinz et al. 1997). However, we acknowledge that specialized cysteine-rich proteins may still require exogenous DTT. We have addressed this in the Discussion.

Reviewer #2 (Recommendations for the authors):

(1) Line 77-78 "we iteratively evaluated the contribution of individual constituents through luciferase reporter assays" - where is all the data? Please use an appropriate figure citation. Figure 1 cherry picks some components, but I think all data should be included.

We have structured the data presentation to show dispensable components in Figure 1 (where removal does not inhibit reaction) and essential components in Figure 2 (where 0-concentration results in zero activity). This ensures a logical flow of the "streamlining" narrative. All raw data for these screenings have been included in the Source Data files.

(2) Line 127 typo "concentrations".

We thank the reviewer for pointing out this error. The typo "concentrations" has been corrected.

(3) Figure 2: "protein expression levels" measured how?/what is the unit of the vertical bar on the right? I'm assuming that this experiment was conducted for discrete concentrations and thus generated discrete data points. However, the graph makes it seem as if this is continuous data. Kindly change the type of graphing to indicate that this is discrete data, showing each data point.

We appreciate the reviewer's suggestion. Protein expression levels were measured using the Nanoluciferase (NLuc) reporter gene assay. We utilized heatmaps/contour plots because our data are bivariate, representing the simultaneous optimization of two concentrations (e.g., Mg²⁺ and K⁺ in Figure 2A). For such matrix-based screenings, heatmaps are significantly more effective than scatter plots at conveying synergistic trends and identifying optimal reaction landscapes. Notably, this visualization approach for discrete biochemical optimization data was successfully employed by Ban lab in their recent study on translation system optimization (Bothe and Ban 2024). The vertical color bar on the right represents the relative expression ratio, normalized to the maximum yield. Although we have provided a scatter plot of this discrete data for reference (see Author response image 1), we believe it appears visually cluttered due to the high density of data points, making it difficult to discern overarching trends. Heatmaps, by contrast, offer a much clearer representation of the optimal reaction landscape. To maintain transparency, the discrete concentration points tested are clearly reflected by the axis ticks, and all raw discrete data are available in the Source Data files.

Author response image 1.

(4) Also, for all figures: the way the units are presented (DTT/mM) is confusing to me; it could just be something like [DTT] (mM).

We have revised all figures and tables to follow the standard format (e.g., [Component] (unit)) as suggested.

(5) Do the sucrose gradient sedimentation data have replicates? If so, please indicate statistics.

The sucrose gradient data provided (Figure 5C) is intended as qualitative evidence that the "fast lysate" method preserves intact 70S ribosomes across different preparation batches. This experiment has been performed independently multiple times with consistent results, demonstrating the high reproducibility of our preparation method. While we did not perform a quantitative comparative analysis of ribosome concentration, the consistency of the peaks confirms the integrity of the translational machinery.

(6) Line 457: fix the red line.

We thank the reviewer for pointing this out. The formatting issue has been resolved in the revised manuscript.

(7) Please mention the limitations of this study in the discussion.

We thank the reviewer for this suggestion. We have added a paragraph to the Discussion addressing the limitations of prokaryotic systems regarding complex eukaryotic post-translational modifications and chaperone requirements.

(8) Please include all uncropped gels in the source data, alongside the raw data, as you have already done.

As requested, we have provided all original, uncropped gel images in the Source Data files, alongside the raw data, to ensure full transparency and compliance with the journal's data sharing policies.

Reviewer #3 (Recommendations for the authors):

(1) The study lacks a comparison of protein levels with a typical cell-free protein synthesis system.

We have performed new quantitative experiments (now included in Figure S3 E-F) to measure absolute protein yields. Our optimized system achieves yields comparable to, or exceeding, several widely recognized highyield protocols while utilizing significantly fewer components. We have also clarified in the text that "highly efficient" refers to the synergistic balance of high yield, low cost, and simplified preparation time.

(2) What do the authors mean by "highly efficient", often used in the manuscript?

We thank the reviewer for the opportunity to clarify our terminology. We have performed new quantitative experiments (now included in Figure S3) to measure absolute protein yields, demonstrating that our optimized system achieves yields comparable to, or exceeding, several widely recognized highyield protocols while utilizing significantly fewer components.

In the context of this manuscript, we use the term "highly efficient" as a holistic descriptor that encapsulates three key dimensions of the system:

(1) Performance Superiority: Achieving higher expression levels and faster kinetics compared to conventional 35-component systems.

(2) Functional Robustness: The ability to efficiently synthesize challenging targets, such as cytotoxic proteins (BsaI) and aggregation-prone proteins (vimentin), which often fail in simplified systems.

(3) Practical Utility: A drastic reduction in preparation time and cost through the "fast lysate" protocol and the removal of 28 auxiliary components, thereby lowering the barrier to adoption.

This definition aligns with the study's core objective: developing a system where efficiency is measured not only by final yield but by the synergy between high performance and extreme ease of use.

(3) In this article, the term 'optimisation' is used as a synonym for 'simplification'. In biochemistry, optimisation commonly refers to an increase in yield, or the same yield achieved more easily or at a lower cost. In this case, however, we have no idea how this new system compares to a conventional expression system in terms of yield.

We thank the reviewer for this conceptual clarification. We agree that in biochemistry, "optimization" typically implies an improvement in yield or cost-effectiveness. In our study, we use the term to describe the process of achieving a superior balance between system simplicity and protein production. To address the reviewer's concern regarding the lack of a direct yield comparison, we have added new data in Figure S3. This figure provides a sideby-side comparison of protein yields between our simplified 7-component system and the conventional 35-component system. The results demonstrate that our system not only matches the performance of the traditional setup but frequently exceeds it in terms of final protein titer, while significantly reducing the reagent cost and preparation complexity. Thus, the simplification achieved in this work represents a true biochemical optimization of the cell-free synthesis process.

(4) The levels of transcripts of the proteins studied were not determined in any of the experiments performed. Therefore, it is unknown whether the effects of different experimental conditions on NLuc, GFP or other protein expression are due to an effect on transcription, translation, or both.

This is an excellent point. We performed a new set of experiments using mRNA templates instead of DNA to isolate the effects on translation (Figure S3G). Our results indicate that while the system's overall boost in NLuc expression is partially attributable to enhanced transcription efficiency, the translation machinery remains highly robust. We have updated the Results and Discussion to reflect this distinction.

References

Bothe, Adrian, and Nenad Ban. 2024. “A Highly Optimized Human in Vitro Translation System.” Cell Reports Methods 4 (4): 100755.

Kigawa, T., T. Yabuki, Y. Yoshida, M. Tsutsui, Y. Ito, T. Shibata, and S. Yokoyama. 1999. “Cell-Free Production and Stable-Isotope Labeling of Milligram Quantities of Proteins.” FEBS Letters 442 (1): 15–19.

Prinz, W. A., F. Aslund, A. Holmgren, and J. Beckwith. 1997. “The Role of the Thioredoxin and Glutaredoxin Pathways in Reducing Protein Disulfide Bonds in the Escherichia Coli Cytoplasm.” The Journal of Biological Chemistry 272 (25): 15661–67.

Yokoyama, Jun, Takayoshi Matsuda, Seizo Koshiba, and Takanori Kigawa. 2010. “An Economical Method for Producing Stable-Isotope Labeled Proteins by the E. Coli Cell-Free System.” Journal of Biomolecular NMR 48 (4): 193–201.

eLife Assessment

This is a valuable study that presents human single nuclei RNA-seq and spatial transcriptomics data of the developing outflow tract and adult aortic valves that will facilitate research in this area. Data presented are solid, with bioinformatics analyses showing cell lineage and trajectory relationships, intriguingly suggesting persistence of embryonic signature in adult aortic valve cells. The latter results would be strengthened by experimental validation.

Reviewer #1 (Public review):

Summary:

The study by Bobola et al reports single nuclear expression analysis with some supporting spatial expression data of human embryonic and fetal cardiac outflow tracts compared to adult aortic valves. The transcription factor GATA6 is identified as a top regulator of one of the mesenchymal subpopulations and potential interacting factors and downstream target genes are identified bioinformatically. Additional bioinformatic tools are used to describe cell lineage relationships and trajectories for developmental and adult cardiac cell types.

Strengths:

The strengths of the study are studies of human tissue and extensive gene expression data that will be valuable to the field.

Weaknesses:

In the revised manuscript the data remain largely correlative since functional relationships in cell lineages and gene regulatory interactions are based on coexpression data and bioinformatic analyses that were not subjected to further validation.

Reviewer #2 (Public review):

Summary:

The manuscript by Leshem et al. presents a transcriptomic analysis of the developing human outflow tract (OFT) at embryonic and fetal stages using snRNAseq and spatial transcriptomic. Additionally, the authors analyze transcriptomic data from the adult aortic valve to compare embryonic and adult cell population, aiming to identify persistent embryonic transcriptional signatures in adult cells. A total of 15 clusters were identified from the embryonic and fetal OFT samples, including three mesenchymal and four endothelial clusters. Using SCENIC analysis on the embryonic snRNAseq data, the authors identified GATA6 as a key regulator of valve precursor cells. Spatial transcriptomic analysis of four fetal OFT sections further revealed the spatial distribution of mesenchymal nuclei, smooth muscle cells, and valvular interstitial cells. Trajectory analysis identified two distinct developmental origins of fetal mesenchymal cells: the neural crest and the second heart field. Finally, the authors used snRNAseq data from the adult aortic valve to propose that embryonic transcriptional signatures persist in a subset of adult cells.

Strengths:

(1) The study offers a rich and detailed dataset, combining snRNA-seq and spatial transcriptomics in human embryonic and fetal OFT, which are challenging to obtain.

(2) The use of SCENIC and trajectory analysis adds mechanistic insight into cell lineage and regulatory programs during valve development.

(3) This study confirms GATA6 ss a key regulator of valve precursor cells.

(4) Comparison between embryonic/fetal and adult datasets represents a novel attempt to trace persistence of developmental transcriptional programs.

Weaknesses:

(1) A major limitation is the lack of experimental validation to support key conclusions, particularly the claim of persistent embryonic transcriptional signatures in adult cells.

(2) The manuscript would benefit from a clearer discussion of how these results advance beyond previous studies in human heart and valve development.

(3) The comparison between embryonic and adult data is interesting but would be more convincing with additional evidence supporting the proposed persistence of embryonic transcriptional signatures in adult cells

Comments on revisions:

The final section of the results concludes with the search for a distribution pattern similar to JAG1. The authors end their article by identifying the FOXC1 and OSR1 genes without providing further validation for their discovery, which is regrettable.

Reviewer #3 (Public review):

Leshem et al have generated a transcriptional cell atlas of the human outflow tract at two developmental timepoints and its adult valvular derivatives. This carefully performed study provides a useful resource for the study of known genes implicated in outflow tract defects and potentially also to discover new disease genes. The authors reveal neural crest and mesodermal contributions to different outflow tract components and show that GATA6, known to play a role in arterial valve development, controls a set of genes expressed in endocardial derived cells during valve development. Interestingly the results reveal intersection with GLI3 and suggest lineage persistence of gene expression through to the adult timepoint, a main new finding of this study.

Comments on revisions:

The authors have carefully addressed previous comments, including the addition of new analysis pointing to potential cooperation between GATA6 and GLI3.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Bobola et al reports single-nucleus expression analysis with some supporting spatial expression data of human embryonic and fetal cardiac outflow tracts compared to adult aortic valves. The transcription factor GATA6 is identified as a top regulator of one of the mesenchymal subpopulations, and potential interacting factors and downstream target genes are identified bioinformatically. Additional bioinformatic tools are used to describe cell lineage relationships and trajectories for developmental and adult cardiac cell types.

Strengths:

The studies of human tissue and extensive gene expression data will be valuable to the field.

Weaknesses:

(1) The expression data are largely confirmatory of previous studies in humans and mice. Thus, it is not clear what novel biological insights are being reported. While there is some novelty and impact in using human tissue, there are extensive existing publications and data sets in this area.

(2) Major conclusions regarding spatial localization, differential gene expression, or cell lineage relationships based on bioinformatic data are not validated in the context of intact tissues.

(3) The conclusions regarding lineage relationships are based on common gene expression in the current study and may not reflect cellular origins or lineage relationships that have previously been reported in genetic mouse models.

(4) An additional limitation is the exclusive examination of adult aortic valve leaflets that represent only a subset of outflow tract derivatives in the mature heart. The conclusion, as stated in the title regarding adult derivatives of the outflow tract, is not accurate based on the limited adult tissue evaluated, exclusive bioinformatic approach, and lack of experimental lineage analysis of cell origins.

Reviewer #2 (Public review):

Summary:

The manuscript by Leshem et al. presents a transcriptomic analysis of the developing human outflow tract (OFT) at embryonic and fetal stages using snRNAseq and spatial transcriptomics. Additionally, the authors analyze transcriptomic data from the adult aortic valve to compare embryonic and adult cell populations, aiming to identify persistent embryonic transcriptional signatures in adult cells. A total of 15 clusters were identified from the embryonic and fetal OFT samples, including three mesenchymal and four endothelial clusters. Using SCENIC analysis on the embryonic snRNAseq data, the authors identified GATA6 as a key regulator of valve precursor cells. Spatial transcriptomic analysis of four fetal OFT sections further revealed the spatial distribution of mesenchymal nuclei, smooth muscle cells, and valvular interstitial cells. Trajectory analysis identified two distinct developmental origins of fetal mesenchymal cells: the neural crest and the second heart field. Finally, the authors used snRNAseq data from the adult aortic valve to propose that embryonic transcriptional signatures persist in a subset of adult cells.

Strengths:

(1) The study offers a rich and detailed dataset, combining snRNA-seq and spatial transcriptomics in human embryonic and fetal OFT, which are challenging to obtain.

(2) The use of SCENIC and trajectory analysis adds mechanistic insight into cell lineage and regulatory programs during valve development.

(3) This study confirms GATA6 as a key regulator of valve precursor cells.

(4) Comparison between embryonic/fetal and adult datasets represents a novel attempt to trace persistence of developmental transcriptional programs.

Weaknesses:

(1) A major limitation is the lack of experimental validation to support key conclusions, particularly the claim of persistent embryonic transcriptional signatures in adult cells.

(2) The manuscript would benefit from a clearer discussion of how these results advance beyond previous studies in human heart and valve development.

(3) The comparison between embryonic and adult data is interesting, but would be more convincing with additional evidence supporting the proposed persistence of embryonic transcriptional signatures in adult cells.

Reviewer #3 (Public review):

Leshem et al have generated a transcriptional cell atlas of the human outflow tract at two developmental timepoints and its adult valvular derivatives. This carefully performed study provides a useful resource for the study of known genes implicated in outflow tract defects and potentially also for discovering new disease genes. The authors reveal neural crest and mesodermal contributions to different outflow tract components and show that GATA6, known to play a role in arterial valve development, controls a set of genes expressed in endocardium-derived cells during valve development. Interestingly, the results suggest lineage persistence of expression of certain genes through to the adult timepoint, a main new finding of this study.

The following points should be addressed to reinforce the conclusions and emphasize the novel features of this study.

(1) It would be helpful to clarify how these new findings confirm or diverge from what is known from analysis of neural crest and mesodermal lineage contributions to different cell populations in the mouse heart. Did the authors identify any human-specific populations of cells, such as the LGR5 population reported by Sahara et al?

(2) The authors should clarify in the introduction and results that they consider the endocardium to be on the SHF trajectory as indicated in Figure S4C. Please add a reference for this point.

(3) The GATA6 results are interesting and support this experimental approach. The paper would be reinforced if the authors could provide any functional validation (in addition to their GATA6 genomic occupancy data) that the designated target genes are regulated by GATA6. This might involve looking at mutant mouse embryos or cultured cells. Do the authors consider that GATA6 may regulate the endocardial to mesenchymal transition during the early stages of valve development? Or the valve interstitial cell versus fibroblast fate choice?

(4) Do the new findings reveal whether human valves have a direct SHF to VIC trajectory (ie, without transiting through endocardium) as has been recently shown in the murine non-coronary valve leaflet? Relevant to this point, Figure 5E appears to show contributions to a single adult aortic valve leaflet - this should be explained, or corrected.

We sincerely thank the Editor and the Reviewers for their constructive and insightful comments. We have carefully addressed the majority of the points raised and believe the revisions have substantially strengthened the manuscript.

Recommendations for the authors:

Reviewing Editor Comments:

Overall, the reviewers felt that integrating these datasets with prior snRNAseq datasets on human OFT (de Bono et al, 2025) would enhance analyses and provide broader context.

Several human fetal heart single-cell datasets have been published, including De Bono et al, 2025. We carefully considered whether integrative analyses with these datasets would further strengthen our study. However, there are substantial differences in anatomical scope: most published datasets encompass broad cardiac regions, whereas our study specifically targets the OFT, enabling higher-resolution characterization of OFT-specific cell states. Integration across datasets with markedly different regional compositions would likely be driven by largescale anatomical differences rather than yield additional OFT-specific insight. In addition, cross-study integration requires batch correction. When datasets differ in anatomical scope, as well as developmental timing, and experimental protocols, stronger correction may be needed, increasing the risk of overcorrection and potential loss of biologically meaningful OFTspecific signals.

Importantly, our dataset has been deposited in the Human Cell Atlas and is fully available for future comparative analyses. We therefore believe that broader cross-dataset integration is best undertaken within such harmonized frameworks as more closely matched datasets become available.

Overall, cluster annotations should be more rigorous, which may be facilitated by comparisons with earlier studies.

We have clarified all the points raised by the reviewer regarding cluster annotation. Specifically: (1) the “cardiac” cluster has been renamed “cardiac muscle” to more accurately reflect its transcriptional identity; and (2) we now explicitly state that mesenchymal populations not resolved in the initial global analysis (across all samples) were subsequently defined through dedicated sub clustering analyses performed separately for the adult and developmental datasets. These clarifications have been incorporated into the revised manuscript.

Citation of other spatial transcriptomics studies on human OFT would be useful.

We apologise for missing these contributions. They have now been added to the text.

Can the authors identify a human-specific population of cells, such as the LGR5 population reported by Sahara et al?

While our dataset does not reveal a novel single-gene marker comparable to the human specific LGR5 marker described for the LGR5-positive population by Sahara et al., it does identify a distinct GATA6-enriched embryonic mesenchymal population that functions as a human valve progenitor lineage. Using regulatory network analysis, RNA velocity, lineage tracing and spatial transcriptomics, we show that this GATA6-driven program is specifically associated with semilunar valve morphogenesis and that its transcriptional signature persists in fetal and adult VIC populations. Thus, the novelty of our study lies in defining this human GATA6-regulated valve progenitor population and its lineage trajectory, rather than in the identification of previously unreported single marker genes.

“….Although we have not defined a novel single-gene marker (analogous to LRG5 [Sahara et al]), our identification of a GATA6 network highlights…..”

Further investigation of the specific role of GATA6 would strengthen findings.

FISH studies would indicate whether GATA6 is involved in EMT or fibroblast versus valve interstitial cell fate choice.

We have added a panel to Fig. S2 (D), showing that GATA6 expression is not restricted to specific outflow tract populations. In CS16-17 embryos, GATA6-expressing nuclei are detected across all embryonic clusters. Given this broad expression pattern, FISH analysis would not distinguish whether GATA6 functions in EMT or in fibroblast versus valve interstitial cell fate specification. While we cannot exclude the possibility that GATA6 contributes to EMT, we observe that its expression levels are highest in cluster 4 (post-EMT) cells. This suggests that GATA6 activation is more likely a consequence of the transition rather than its initiating cause (shown in Fig. S2D).

Functional validation of some proposed GATA6 targets would strengthen findings.

To our knowledge, there are currently no publicly available datasets defining the GATA6 regulatory network in human OFT cells or valvular fibroblast progenitors. Existing datasets focus primarily on cardiomyocytes, which arise from a distinct developmental lineage. Given the well-established cell-type and context dependence of transcription factor activity, these datasets are unlikely to provide meaningful insight into regulatory relationships within the valvular lineage examined here.

As noted in the original submission, we previously leveraged published mouse GATA6 ChIPseq data from E11.5 OFT (DOI: https://doi.org/10.7554/eLife.31362) as independent support for the GATA6 regulon identified in our human dataset. In this revised version, we have now extended this analysis by formally quantifying the overlap between the cluster 4 GATA6 regulon and genes bound by GATA6 in the mouse OFT dataset. Using a hypergeometric enrichment test, we found that the observed overlap is approximately two-fold greater than expected by chance and highly significant (p = 1.2 × 10^-33). This statistical analysis strengthens our original interpretation and provides quantitative support that the identified regulon is strongly enriched for bona fide GATA6-bound targets in a closely related developmental context.

In addition, we examined the spatial expression pattern of the GATA6 regulon gene set and found that it specifically localizes to the semilunar valves (OFT derivatives), consistent with GATA6 activity in this developmental context. This new analysis has been incorporated into Figure 2F of the revised manuscript.

Collectively, the cross-species binding enrichment and valve-specific expression pattern provide orthogonal support for the biological relevance of the identified GATA6 regulon and strengthen the mechanistic interpretation of GATA6 function in OFT and valve development.

As GATA6 has been previously identified in mouse studies, can the authors identify novel transcription factors potentially involved in OFT development?

To identify additional transcription factors potentially involved in OFT development and to define regulators that may confer specificity to GATA6 activity, we compared the GATA6 regulon with the regulons of other cluster 4 transcription factors identified by SCENIC (SOX4, GLI3, RARG, ETV1, GLIS3, BACH2, ZNF423, FOXO3, ZBTB20).

While all cluster 4 regulators share some downstream targets, GLI3 regulon showed approximately twice the degree of overlap with the GATA6 regulon compared to the other factors. This suggests a potential functional interaction between GATA6 and GLI3 in OFT associated mesenchyme. Consistent with this, cooperation between GATA6 and GLI3 has been reported in mouse limb development. These findings have now been incorporated into the Results section, and co-expression of GATA6 and GLI3 in CS16-17 populations is shown in Figure S2DE.

Although GATA6 has previously been implicated in OFT development, SCENIC analysis provides mechanistic insight by defining the downstream gene programs active in specific human embryonic lineages. Thus, the novelty of our findings lies not in re-identifying GATA6, but in characterizing its regulon in human OFT- and valve-associated mesenchyme and identifying potential cooperating regulators such as GLI3.

Embryonic signatures in adult valve cells are an interesting finding, that should be further explored by pseudotime trajectories, which may also indicate whether SHF cells have a direct trajectory to VIC (without transiting endocardium), as recently shown in mice.

We included all embryonic populations, including cardiac progenitor cells (SHF), in the pseudotime trajectory analysis. However, we did not observe evidence of a direct trajectory from SHF cells toward VIC. In contrast, the same analysis consistently identified a trajectory linking endocardial cells to VIC, supporting an endocardial origin in our dataset.

Reviewer #1 (Recommendations for the authors):

(1) Major conclusions regarding cell lineages and derivatives are based on common gene expression patterns and bioinformatic tools. Thus, these conclusions are not based on empirical data, and assumptions regarding lineages based on gene expression may not be accurate. The language related to lineage analysis, derivative, and longitudinal gene expression is not supported by data. For example, studies in mice have shown that aortic valve interstitial cells from endocardial cushions and neural crest-derived lineages have overlapping patterns of ECM gene expression and cannot be easily distinguished in adults. Thus, it is not possible to determine derivation and cell origins based on gene expression alone.

While we fully acknowledge that gene expression-based analyses provide correlative rather than direct lineage-tracing evidence, the Reviewer’s statement that “it is not possible to determine derivation and cell origins based on gene expression alone,” and the example cited in support, appear to equate global transcriptional similarity with the distinct embryonic transcriptional signatures that underpin our analysis.

As the Reviewer notes, a given differentiated cell type can derive from different embryonic progenitors. Due to functional convergence, differentiated cells often exhibit highly similar expression profiles that reflect their shared function rather than developmental origin. Consequently, discriminating embryonic origins based on global expression profiles, or even for highly distinctive genes of differentiated cells, is very challenging. The example cited by the Reviewer - overlapping ECM gene expression in aortic valve interstitial cells derived from endocardial cushions and neural crest - illustrates precisely this point.

However, our analysis does not rely on global transcriptional similarity or on markers of mature differentiated cells. Instead, we specifically identified gene sets that are highly distinctive of embryonic clusters prior to the onset of differentiation. These signatures are enriched for transcription factors and signaling molecules that define developmental identity, rather than functional effector genes associated with mature cell states. We have shown that these embryonic signatures persist in fetal cells (which already express differentiated markers but are developmentally closer to the embryonic stage relative to adult cells) and remain detectable, albeit attenuated, in adult cells. It is these distinctive embryonic transcriptional signatures, rather than global or shared functional gene expression, that we have used to infer potential lineage relationships.

We fully acknowledge that this constitutes correlative evidence rather than direct lineage tracing, which is not feasible in human studies. However, the persistence of embryonic regulatory signatures into fetal and adult stages provides a biologically plausible link to developmental origin. This persistence most plausibly reflects partial retention of ancestral embryonic transcriptional programs in descendant cells, rather than de novo activation later in life of embryonic genes that were never previously expressed in that cell’s lineage.

(2) Most of the findings related to cell composition, gene expression, and cell lineages seem to be largely confirmatory of previous reports. Novel findings should be emphasized and validated in the tissues.

We agree that several aspects of our dataset reproduce and extend findings from previous human and animal studies, which we regard as an important validation of the atlas. However, our study also provides multiple novel insights that are directly supported by our spatial data. Specifically, we (i) identify a GATA6-enriched embryonic mesenchymal valve progenitor population, (ii) delineate its GATA6 transcriptional regulon and direct targets implicated in OFT and valve disease, and (iii) trace its embryonic transcriptional signature into fetal and adult valve interstitial cell populations. These findings are strengthened by our spatial transcriptomic data, which maps the GATA6 regulon and key targets to the semilunar valves and adjacent arterial root, providing in situ validation of both cell identity and gene expression patterns (see Fig. 3 and the newly added Fig. 2F). We have revised the Discussion to more explicitly highlight these novel aspects and their spatial validation in the final

“In summary, our work goes beyond confirming previously reported cell types by (i) defining a GATA6-regulated human valve progenitor lineage and its descendants, (ii) establishing distinct embryonic origins for smooth muscle and valvular fibroblasts, and (iii) demonstrating persistence of embryonic signatures in adult valve cell populations. These findings are directly supported in tissue by our spatial transcriptomics data, which map these lineages and regulatory programs to defined anatomical domains within the human OFT and semilunar valves.”

(3) The developing outflow tract of the heart contributes to more than just the aortic valve leaflets in adults. Additional conotruncal structures need to be evaluated in order to define adult derivatives of the developing outflow tract as described in the title.

The title has been changed to reflect that only adult aortic valves were examined.

(4) Major conclusions regarding the GATA6 regulatory network and downstream target genes are not validated in the context of the developing outflow tract or adult valves. Is GATA6 expression restricted to specific outflow tract populations? Is GATA6 binding or responsive gene expression detected for the indicated target genes?

We performed additional analyses that further reinforce the relationship between GATA6 and its target genes and support the biological relevance of GATA6 downstream targets in arterial valve development. Below, we address the specific questions raised by the reviewer.

(1) Is GATA6 expression restricted to specific outflow tract populations?

GATA6 expression is not restricted to specific outflow tract populations. In CS16-17 embryos, GATA6-expressing cells are detected across all embryonic clusters; however, expression levels are highest in cluster 4 (valve precursor cells).

Despite this broad expression pattern, SCENIC identifies GATA6 activity (i.e., a GATA6 regulon) specifically in cluster 4. This apparent restriction of GATA6 regulatory activity to cluster 4 may be explained, at least in part, by its elevated expression levels within this cluster. Alternatively, given that transcription factors often act in a combinatorial manner, GATA6 may co-regulate its target genes in cluster 4 together with additional cluster-specific regulators. To explore this possibility, we compared the GATA6 regulon with the regulons of other cluster 4 transcription factors identified by SCENIC (namely SOX4, GLI3, RARG, ETV1, GLIS3, BACH2, ZNF423, FOXO3, ZBTB20) in order to identify potential co-regulatory modules. As expected, since these regulons are sampled from the subset of genes enriched in cluster 4, all regulators share a substantial proportion of downstream targets with GATA6. However, GLI3 stands out, showing approximately twice the degree of overlap compared to the other factors. This suggests a functional interaction between GATA6 and GLI3, consistent with previously reported cooperation in mouse limb development. These results have been incorporated into the Results section, and the expression of GATA6 and GLI3 in CS16-17 cell populations is shown in Fig. S2DE.

(2) Is GATA6 binding or responsive gene expression detected for the indicated target genes?

We were unable to find public data describing the GATA6 regulatory network or its downstream targets in the specific human cell types examined here (OFT cells; valvular fibroblast progenitors). Available datasets focus primarily on cardiomyocytes, which arise from a distinct lineage, and because transcription factor function is highly cell-type and context dependent, these datasets are unlikely to be helpful in inferring regulatory relationships in the valvular lineage.

The strongest validation for the GATA6 regulon identified in this study comes from the mouse GATA6 occupancy data (this was included in the original manuscript). Although derived from a different species, GATA6 binding has been profiled in a highly related developmental context, the OFT. To assess the relevance of these data to our human findings, we performed a hypergeometric test comparing the GATA6 regulon identified in cluster 4 (this study) with genes bound by GATA6 in E11.5 mouse OFT ChIP-seq data (DOI: https://doi.org/10.7554/eLife.31362). The observed overlap is substantially greater than expected by chance: it is approximately twice the expected value, and the enrichment is highly significant (p = 1.2 × 10^-33). Biologically, this strongly supports the interpretation that many genes within GATA6 regulon are likely to be direct GATA6 targets, or at minimum are strongly associated with GATA6 binding, rather than representing a random gene set. This analysis has been added to the revised manuscript.

In this revised version of the manuscript, we also overlapped the expression of GATA6 regulon genes to our fetal spatial transcriptomics data. GATA6 regulon was identified in embryonic cluster 4, whose expected trajectory is fetal valvular fibroblasts (cluster 12). Remarkably, GATA6 regulon genes are expressed in both the aortic and pulmonary valves, and their expression pattern aligns closely with HAPLN1-positive valvular fibroblasts (cluster 12), further supporting the biological relevance of this gene set. This new data has been added to Fig 2(F).

Together, the strong enrichment of GATA6 regulon genes among GATA6-bound targets in the OFT, and the specific expression of this gene set within the arterial valves (cluster 4 descendant cells), support the biological relevance of GATA6 downstream targets in arterial valve development and disease. In addition, we identify GLI3 as a potential GATA6 co-binding partner.

(5) What are "cardiac" cell types in the embryonic single cell clustering? Are these cardiomyocytes? Cardiac is an ambiguous term if the cells being analyzed are all in the heart.

Thank you for highlighting this ambiguity. The “cardiac” population refers specifically to cardiac muscle cells. We have updated the labels in Fig. 1E, 1F, and Fig. S3A to make this explicit.

(6) The methods and analytical tools seem fairly standard for single nuclear gene expression and spatial genomics studies. What are the new tools and resources being reported? The "novel lineage tracing algorithm" mentioned in the methods is not well described. A Cellxgene VIP app is mentioned, but is not described in detail. Also, it seems to be housed on a local server, which is not optimal.

The description of the lineage tracing algorithm has been expanded in the method’s section of the paper.

The data has been submitted to the Human Cell Atlas, a coordinated global effort to systematically map human cell types using standardized, interoperable formats. Public access via cell x gene enables interactive visualization, gene-level queries, and cross-dataset comparisons without requiring advanced computational expertise. This broad accessibility enhances reproducibility, facilitates integration with complementary single-cell and spatial datasets, and maximizes the visibility, transparency, and long-term impact of our work.

(7) Only adult aortic valves from females were included in the study.

The rationale for using female tissues has been explained in the result section:

We collected female samples to mitigate individual variability and maximise the possibility to analyse healthy aortic valves, justified by the lower incidence and severity of aortic disease in females versus males.

(8) In many of the figures, the font size of the text is too small to read.

We have increased the font size in all figures where this was compatible with the layout. For the larger plots, additional enlargement would necessitate scaling the panels beyond the allowable page dimensions, and therefore could not be implemented.

(9) "CAT" is not a commonly used abbreviation for congenital heart anomalies related to persistent truncus arteriosus.

CAT is now the preferred term for PTA as latinised terms are no longer used.

Reviewer #2 (Recommendations for the authors):

Overall, this study is thoughtfully conducted and offers valuable observations that contribute to our understanding of valve morphogenesis. However, my main concern is the lack of experimental validation to support the findings, particularly the conclusion regarding the persistence of transcriptional signatures in adult cells, which is not sufficiently substantiated or clearly argued. It is unclear how this study advances beyond previous research in humans.

Major points:

(1) Several recent studies have applied spatial transcriptomics to human embryonic and fetal hearts, including OFT (Asp et al., 2019; Queen et al., 2023; Farah et al., 2024; De Bono et al., 2025). It is disappointing that the authors did not acknowledge these important contributions.

We apologise for missing these contributions. They have now been added to the text.

(2) The present study used snRNAseq to explore the transcriptional signature of the fetal OFT. A similar approach was used by De Bono et al. (2025) to analyze fetal hearts. Integrating these complementary snRNAseq datasets could enhance the current analysis and provide broader context for the findings.

The reviewers suggested that integrating our datasets with prior snRNA-seq datasets on human OFT (de Bono et al., 2025) could enhance the analyses and provide broader context. While several fetal heart datasets have been published (e.g., Sahara et al.), our study focuses specifically on the OFT. These other studies do not perform cross-dataset comparisons. We therefore do not see a strong rationale for integrating ours, especially given that those datasets cover much larger regions of the heart.

(3) Figure 1 presents 18 distinct clusters identified through unsupervised clustering. The authors classify three of these clusters broadly as mesenchymal cells. However, the term "mesenchymal cells" lacks precision. The authors should clarify why these clusters were not more specifically defined as fibroblasts or myofibroblasts based on marker expression.

Clustering of the full dataset does not provide sufficient resolution to distinguish all mesenchymal cell types. The clusters broadly annotated as mesenchymal comprise heterogeneous populations, including both undifferentiated embryonic mesenchymal cells and more differentiated fetal mesenchymal cells. These mesenchymal clusters were therefore further subclustered, and the resulting cell identities are described in detail in the Results sections corresponding to Fig. 2 and Fig. 3.

(4) The authors used SCENIC on their snRNAseq datasets to infer key cell fate regulators and identified GATA6 as a top regulator of embryonic mesenchymal cluster 4. However, the rationale for focusing on GATA6, which is already known to be associated with CHD in humans, is not fully convincing. Why not investigate a transcription factor whose role in valve development remains unexplored?

There are two key outcomes from a SCENIC analysis: (1) the identification of major transcriptional regulators driving the differentiation of a given cluster, and (2) the identification of their regulons (the downstream gene programs they control). While GATA6 is indeed already known to be associated with CHD in humans, including valve malformations and major OFT defects, its downstream targets in the relevant human developmental lineages have not been defined. Understanding these targets is essential for clarifying the molecular basis of GATA6-mediated CHD. Thus, the significance of our result does not lie in the rediscovery of GATA6 as a CHD-related factor, but in identifying the genes it regulates in embryonic OFT- and valve-associated mesenchyme. These GATA6-controlled genes in the OFT and valves represent biologically plausible candidate genes for human OFT defects, as disruption of GATA6 targets could similarly contribute to CHD.

In this revised version we have performed a hypergeometric test showing that GATA6 regulon genes are significantly enriched among genes bound by GATA6 in the OFT. Biologically, this strongly supports the interpretation that many genes within the GATA6 regulon are likely to be direct GATA6 targets, or at minimum are strongly associated with GATA6 binding in the OFT, rather than representing a random gene set.

We have also mapped the expression of GATA6 regulon to the semilunar valves. Collectively, these analyses demonstrate that the GATA6 regulon captures a biologically coherent and developmentally relevant program, offering new mechanistic insight into how GATA6 influences OFT and valve formation and how its disruption may contribute to CHD.

(5) Several studies have already suggested a role for GATA6 in EMT. Do the authors propose that GATA6 regulates this process during embryonic valve development? Once again, validation using FISH would be important to support these findings.

We do not propose that GATA6 directly regulates EMT during embryonic valve development. We rather make two independent observations: (1) cluster 4 derives from cluster 7 (likely through EMT); (2) GATA6 regulates cluster4-specific genes.

The first observation is supported by RNA velocity, which links cluster 7 to cluster 4. Supporting this interpretation, endothelial cluster 7 is enriched for genes associated with arterial valve development, and mesenchymal cluster 4 cells are identified as progenitors of fetal valve fibroblasts. Because cluster 7 is endothelial and cluster 4 is mesenchymal, this trajectory suggests an endothelial-to-mesenchymal transition.

Second, SCENIC analysis identifies GATA6 as a regulator of cluster 4 genes. Additionally, the GATA6 regulon shows distinct localization to the formed valves in fetal cells (new data added to Fig 2F). Together these findings support the notion that GATA6 regulates a gene program specific to the cell populations that will give rise to the valves and that these genes remain selectively expressed in valve cells once the arterial valves have formed.

While we cannot exclude the possibility that GATA6 contributes to EMT, we observe that GATA6 expression levels are highest in cluster 4 (post-EMT) cells, suggesting that its activation may be a consequence of the transition rather than its initiating cause (now shown in Fig S2D).

For validation using FISH, please see response to point 6 below

(6) I found it curious that the ST section was used to validate MECOM expression (Figure 2I), while ST had not yet been introduced at this point in the manuscript. Validation using FISH would have been a more appropriate approach.

Thank you for drawing attention to this discrepancy. Spatial transcriptomics is now introduced before MECOM analysis, in the Results section pertaining to Figure 2F

“…spatial transcriptomic analysis of a later stage (12pcw) OFT shows that GATA6 regulon is mainly restricted to the aortic and pulmonary valves (Fig 2F)”.

With regard to this and the above comment concerning FISH, while RNA FISH/RNAscope would provide an additional orthogonal approach, the Visium-based spatial transcriptomics platform directly measures MECOM transcripts in tissue sections and, in our view, represents an appropriate and sufficiently sensitive method for validating its spatial distribution in the human OFT. We have therefore relied on the spatial transcriptomics dataset to confirm and validate gene expression patterns, rather than performing additional FISH experiments. We now explicitly state that this approach serves as an independent in situ validation of gene expression, including MECOM.

(7) "Spatial resolution of mesenchymal nuclei in the OFT" section: It is unclear which cluster the authors are referring to in this section.

As mentioned in the text, we “mapped the five fetal mesenchymal clusters to distinct structures in the OFT” and used distinctive markers to confirm spatial assignments.

(8) The authors should justify their choice to use Cell2location instead of a deconvolution method.

We selected cell2location because it provides a probabilistic, hierarchical Bayesian framework that explicitly models technical variability across both single-cell reference data and spatial transcriptomics platforms. Rather than relying on predefined marker genes or simple linear regression, cell2location leverages the full transcriptomic profile of reference single-cell data and incorporates a factor analysis-based framework to model shared transcriptional signatures and latent structure across cell types. This approach improves discrimination between closely related cell states and reduces sensitivity to gene selection bias. Additionally, the probabilistic formulation yields uncertainty estimates for inferred cell abundances, enhancing interpretability and statistical rigor. Together, these features make cell2location particularly well suited for resolving complex cellular composition in our fetal human tissue spatial transcriptomics data.

(9) Figure 3: Cluster 9 is identified as endothelial, yet it includes markers such as MYH11 among its top genes, a gene more commonly associated with cells at the base of the aorta. This raises questions about the accuracy of the cluster annotation.

We could not find the definition of cluster 9 as endothelial to which the reviewer refers to. In Fig 3, both in the result text and in the figure legend, cluster 9 is identified as smooth muscle, which is consistent with MYH11 expression. The endothelial cluster is shown in Fig S3C.

(10) The approach used to trace embryonic signatures in adult cells, based on overlap with the top 100 genes in embryonic clusters, relies largely on gene expression similarity, without incorporating lineage inference tools such as RNA velocity or pseudotime analysis. This limits the ability to distinguish true developmental relationships from shared functional programs. I believe that the use of aggregated adult samples may mask individual variability. Validation in separate samples (AV1 and AV3) lacks statistical rigor. The observed lower expression of embryonic genes in adult cells further complicates interpretation, raising the possibility that these signatures reflect residual expression rather than persistent lineage markers.

We thank the reviewer for the opportunity to clarify our approach.

We fully agree that tools such as RNA velocity and pseudotime are powerful for capturing short-term dynamic transcriptional changes and inferring lineage trajectories within continuous developmental processes. Indeed, we applied RNA velocity and identified a transition between clusters 7 and 4 in embryonic cells (Fig 2). However, as noted in the Results section, “trajectory inference methods failed to establish lineage relationships between embryonic and fetal populations”. These methods assume temporal continuity and comparable transcriptional kinetics between cells. When comparing samples separated by large developmental intervals (e.g., embryonic versus adult tissues), these assumptions do not hold: RNA velocity vectors become unreliable and may even yield biologically meaningless directions. Therefore, rather than forcing a continuous trajectory across temporally distant datasets, we employed an anchoring approach designed to identify conserved transcriptional programs and potential lineage correspondences between embryonic and adult cell types.

To address the concern about individual variability, we performed analyses both on aggregated adult samples and on individual replicates (AV1 and AV3). The results were highly consistent across both levels of analysis, and statistical significance was supported by very low p-values, indicating that the observed patterns are robust and reproducible. We therefore believe our analysis in independent samples is statistically sound.

Finally, we agree that adult cells display lower expression of embryonic genes, and we acknowledge that these signatures may represent residual rather than persistent expression. This observation aligns with our intended interpretation: our goal was not to demonstrate enduring embryonic marker expression, but to highlight that adult cells retain transcriptional traces that connect them to their developmental origins.

Reviewer #3 (Recommendations for the authors):

(1) Please clarify if MEIS1, JAG1, ROR1, PRDM6 have been previously implicated in neural crest cell development. Are these then new potential regulators of neural crest cells? The same applies to SOX6 for the mesodermal population.

The main reason for selecting these genes (MEIS1, JAG1, ROR1, and PRDM6 in cluster 20, and SOX6 in cluster 4) is that they serve as distinctive markers of specific embryonic clusters. Because their expression remains restricted at later developmental stages, they allow reliable tracing of bona fide descendant cells originating from cluster 20 and cluster 4 into fetal and adult tissues. Importantly, MEIS1, JAG1, ROR1, and PRDM6 were not chosen as new potential regulators of neural crest (NC) cells, but rather because their expression is enriched in cluster 20 and remains restricted at later developmental stages, allowing reliable tracing of bona fide descendant cells originating from cluster 20. Since cluster 20 is, based on transcriptional profiles, the embryonic mesenchymal cluster most closely related to the NC lineage, these markers enable lineage tracing of NC-descendent cells. Nonetheless, these genes have all been linked to neural crest biology, either through known functional roles or through specific expression patterns associated with NC development.

Similarly, SOX6 was selected for its restricted expression in cluster 4, a pattern that is preserved in its descendant populations, making it a suitable marker for tracking the mesoderm-derived lineage.

(2) Please comment in the text whether any regional transcriptional differences (rather than cell type differences) were detected between the aortic and pulmonary regions.

We have added the following text to the result section related to Fig 3: “No molecular differences or distinguishing markers were identified between the aortic and pulmonary valves.”

(3) There appear to be no myocardial cells in the adult valve tissue - the authors could discuss what the fate of myocardium is in the embryonic OFT. Are they only looking at a subset of derivatives of the embryonic OFT?

Our adult dataset represents the aortic valve complex and adjacent arterial root tissue (a subset of outflow tract derivatives) rather than the entire outflow tract (this has now been specified in the title). Spatial transcriptomic analysis identified myocardial gene expression within the ventricular and outflow tract walls at CS16-19, but not within the valve leaflet cluster (Queen et al., 2023). This is consistent with previous observations that myocardium contributes to the arterial root and supports early cushion formation, but does not persist in mature valve tissue, which becomes predominantly fibrous and populated by valve interstitial cells. This explanation has been added to the analysis of cell populations in the valves.

(4) Please equate Carnegie stages 13-23 to embryonic days or weeks of gestation in the first paragraph to help the general reader.

We have added the suggested clarification and noted that this period spans four weeks of human development, rather than the three weeks previously indicated. The text has been updated accordingly.

(5) I suggest rewriting the first sentence of the introduction using the plural, as there are many different types of CHD.

The sentence has been changed accordingly.

(6) It would be helpful to add the persistence of embryonic signatures into adult valve cell types in Figure 4E.

We thank the reviewer for this helpful suggestion. To address this point, we have now added an analysis of the persistence of embryonic signatures in adult valve cell types to Figure 4E. Specifically, we selected 10 representative genes from the 100-gene embryonic signature lists of cluster 4 and cluster 20 and projected their expression onto the t-SNE shown in Figure 4E. The combined (module) expression of these 10 genes is now shown in Figure S6E, and the expression of the individual genes is presented in the newly added Figure S7.

We would like to clarify that our statistical framework identifies potential descendant populations based on significant enrichment of an embryonic gene signature. Therefore, individual embryonic genes are not necessarily expected to be expressed exclusively or uniformly within a single adult population.

(7) Please explain how the 2-dimensional plot in 2J relates to the other plots.

The plot originally shown in Fig 2J (now Fig 2K) was generated by applying RNA velocity exclusively to CS16-17 nuclei. Developmental nuclei (excluding adult samples) were subclustered as shown in Fig S2AB, resulting in the 5 clusters of embryonic nuclei analysed in Fig 2J: cardiac muscle (2, 17), endothelial (7), and mesenchymal (4, 20).

eLife Assessment

This important study examines the potential role of ARHGAP36 transcriptional regulation by FOXC1 in controlling sonic hedgehog signaling in human neuroblastoma. While there are many solid findings that strongly support this signaling pathway, there are some aspects of the study that are underdeveloped, particularly the generalizability in the context of cancer cells.

Reviewer #1 (Public review):

This thoughtful and thorough mechanistic and functional study reports ARHGAP36 as a direct transcriptional target of FOXC1 which regulates Hedgehog signaling (SUFU, SMO, and GLI family transcription factors) through modulation of PKAC. Clinical outcome data from patients with neuroblastoma, one of the most common extracranial solid malignancies in children, demonstrate that ARHGAP36 expression is associated with improved survival. Although this study largely represents a robust and near-comprehensive set of focused investigations on a novel target of FOXC1 activity, several significant omissions undercut the generalizability of the findings reports.

(1) It is notable that the volcano plot in Fig. 1a does now show evidence of canonical Hedgehog gene regulation even though the subsequent studies in this paper clearly demonstrate that ARHGAP36 regulates Hedgehog signal transduction. Is this because canonical Hedgehog target genes (GLI1, PTCH1, SUFU) simply weren't labeled? Or is there a technical limitation that needs to be clarified? A note about Hedgehog target genes is made in conjunction with Table S1, but the justification or basis of defining these genes as Hedgehog targets is unclear. More broadly, it would be useful to see ontology analyses from these gene expression data to understand FOXC1 target genes more broadly. Ontology analyses are included in a supplementary table, but network visualizations would be much preferred.

(2) Likewise, the ChIP-seq data in Fig. 2 are under-analyzed, focusing only on the ARHGAP36 locus and not more broadly on the FOXC1 gene expression program. This is a missed opportunity that should be remedied with unbiased analyses intersecting differentially expressed FOXC1 peaks with differentially expressed genes from RNA-sequencing data displayed in Fig. 1.

(3) RNA-seq and ChIP-seq data strongly suggest that FOXC1 regulates ARHGAP36 expression, and the authors convincingly identify genomic segments at the ARHGAP36 locus where FOXC1 binds, but they do not test if FOXC1 specifically activates this locus through the creation of a luciferase or similar promoter reporter. Such a reagent and associated experiments would not only strengthen the primary argument of this investigation but could serve as a valuable resource for the community of scientists investigating FOXC1, ARHGAP36, the Hedgehog pathway, and related biological processes. CRISPRi targeting of the identified regions of the ARHGAP locus is a useful step in the right direction, but these experiments are not done in a way to demonstrate FOXC1 dependency.

(4) It would be useful to see individual fluorescence channels in association with images in Fig. 3b.

(5) Perhaps the most significant limitation of this study is the omission of in vivo data, a shortcoming the authors partly mitigate through the incorporation of clinical outcome data from pediatric neuroblastoma patients in the context of ARHGAP36 expression. The authors also mention that high levels of ARHGAP36 expression were also detected in "specific CNS, breast, lung, and neuroendocrine tumors," but do not provide clinical outcome data for these cohorts. Such analyses would be useful to understand the generalizability of their findings across different cancer types. More broadly, how were high, medium, and low levels of ARHGAP36 expression identified? "Terciles" are mentioned, but such an approach is not experimentally rigorous and RPA or related approaches (nested rank statistics, etc) are recommended to find optimal cutpoints for ARHGAP36 expression in the context of neuroblastoma, "specific CNS, breast, lung, and neuroendocrine" tumor outcomes.

Comments on revisions:

I am underwhelmed by this revision, for which I recommended more visualizations of already-generated bioinformatic data that the authors have not provided. Some attempts were made (e.g. network analysis), but other suggestions for improvement were not incorporated (e.g. more comprehensive ChIP-seq analysis). Beyond these relatively straightforward missed opportunities for improvement, there remains a lack of in vivo data and the clinical relevance of these findings are unclear due to potential sources of bias in the data sets analyzed.

Reviewer #2 (Public review):

FOXC1 is a transcription factor essential for the development of neural crest-derived tissues and has been identified as a key biomarker in various cancers. However, the molecular mechanisms underlying its function remain poorly understood. In this study, the authors used RNA-seq, ChIP-seq, and FOXC1-overexpressing cell models to show that FOXC1 directly activates transcription of ARHGAP36 by binding to specific cis-regulatory elements. Elevated expression of FOXC1 or ARHGAP36 was found to enhance Hedgehog (Hh) signaling and suppress PKA activity. Notably, overexpression of either gene also conferred resistance to Smoothened (SMO) inhibitors, indicating ligand-independent activation of Hh signaling. Analysis of public gene expression datasets further revealed that ARHGAP36 expression correlates with improved 5-year overall survival in neuroblastoma patients. Together, these findings uncover a novel FOXC1-ARHGAP36 regulatory axis that modulates Hh and PKA signaling, offering new insights into both normal development and cancer progression.

Main strengths of the study are:

(1) Identification of a novel signaling pathway involving FOXC1 and ARHGAP36, which may play a critical role in both normal development and cancer biology. 2) Mechanistic investigation using RNA-seq, ChIP-seq, and functional assays to elucidate how FOXC1 regulates ARHGAP36 and how this axis modulates Hh signaling. 3) Clinical relevance demonstrated through analysis of neuroblastoma patient datasets, linking ARHGAP36 expression to improved 5-year overall survival.

Comments on revisions:

Consider adding subsection titles to the Results section to better organize the findings and improve readability.

The authors may consider adding a statement in paragraph 4 of the Results section or in the Discussion noting that ARHGAP36 has been reported to inhibit PKAC activity and promote PKAC degradation.

Reviewer #3 (Public review):

Summary:

The focus of the research is to understand how transcription factors with high expression in neural crest cell derived cancers (e.g., neuroblastoma) and roles in neural crest cell development function to promote malignancy. The focus is on the transcription factor FOXC1 and using murine cell culture, gain- and loss of function approaches and ChIP profiling, among other techniques, to place PKC inhibitor ARHGAP36 mechanistically between FOXC1 and another pathway associated with malignancy, Sonic Hedgehog (SHH).

Strengths:

Major strengths are the mechanistic approaches to identify FOXC1 direct targets, definitively showing that FOXC1 transcriptional regulation of ARHGAP36 leads to dysregulation of SHH signaling downstream of ARHGAP36 inhibition of PKC. Starting from a screen of Foxc1 OE to get to ARHGAP36 and then using genetic and pharmacological manipulation to work through the mechanism is very well done. There is data that will be of use to others studying FOXC1 in mesenchymal cell types, in particular the FOXC1 ChIP-seq.

Weaknesses:

Work is almost all performed in NIH3T3 or similar cells (mouse cells, not patient or mouse-derived cancer cells) so the link to neuroblastoma that forms the major motivation of the work is not clear. The authors look at ARHGAP36 levels in association the neuroblastoma patient survival however the finding, though interesting and quite compelling, is misaligned with what the literature shows about FOXC1 and SHH, their high expression is associated with increased malignancy (also maybe worse outcomes?). Therefore, ARHGAP36 expression may be more complicated in a tumor cell or may be unrelated to FOXC1 or SHH, leaving one to wonder what the work in NIH3T3 cells, though well done, is telling us about the mechanisms of FOXC1 as an oncogene in neuroblastoma cells or in any type of cancer cell. Does it really function as a SHH activator to drive tumor growth? The 'oncogenic relevance' and 'contribution to malignancy' claimed in the last paragraph of the introduction is currently weakly supported with the data as presented. This could be improved with studying some of these mechanisms in patient-derived neuroblastoma cells with high FOXC1 expression. Does inhibiting FOXC1 change SHH and ARHGAP36 and have any effect on cell proliferation or migration? Alternatively, does OE of FOXC1 in NIH3T3 cells increase their migration or stimulate proliferation in some way and is this dependent on ARHGAP36 or SHH? Application of their mechanistic approaches in cancer cells or looking for hallmarks of cancer phenotypes with FOXC1 OE (and dependent on SHH or ARHGAP36) could help to make a link with cellular phenotypes of malignant cells.

In the revised manuscript, the authors did not add studies in any malignant cell type (mouse or human, neuroblastoma or other) with Foxc1 overexpression to test if the mechanisms they identify in the mouse fibroblasts is present in cancer cells nor if this relates to cellular phenotypes of malignancy (migration or proliferation). Therefore strengths and weaknesses identified by this reviewer in the prior version are the same.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This thoughtful and thorough mechanistic and functional study reports ARHGAP36 as a direct transcriptional target of FOXC1…… Although this study largely represents a robust and near-comprehensive set of focused investigations on a novel target of FOXC1 activity, several significant omissions undercut the generalizability of the findings reported.

(1) It is notable that the volcano plot in Figure 1a does now show evidence of canonical Hedgehog gene regulation, even though the subsequent studies in this paper clearly demonstrate that ARHGAP36 regulates Hedgehog signal transduction. Is this because canonical Hedgehog target genes (GLI1, PTCH1, SUFU) simply weren't labeled? Or is there a technical limitation that needs to be clarified? A note about Hedgehog target genes is made in conjunction with Table S1, but the justification or basis of defining these genes as Hedgehog targets is unclear. More broadly, it would be useful to see ontology analyses from these gene expression data to understand FOXC1 target genes more broadly. Ontology analyses are included in a supplementary table, but network visualizations would be much preferred.

Space constraints precluded labelling the Volcano plot with all 285 significantly differentially expressed genes. So rather than just Hedgehog pathway members, the most dysregulated were labelled (those with a 4-fold change: -2 <log\_2\> +2) and the full list of DEGs provided in the supplemental excel file. We have added the suggested network analysis, and for additional rigor also included protein interaction partners of Gli1 and Arhgap36 (Fig. S12).

(2) Likewise, the ChIP-seq data in Figure 2 are under-analyzed, focusing only on the ARHGAP36 locus and not more broadly on the FOXC1 gene expression program. This is a missed opportunity that should be remedied with unbiased analyses intersecting differentially expressed FOXC1 peaks with differentially expressed genes from RNA-sequencing data displayed in Figure 1.

We agree that genome-wide analysis of ChIP-seq data from Foxc1 over-expression is worthwhile, not least for diverse malignancies where FOXC1 is over-expressed. We chose to restrict the focus of this paper in order to define, as comprehensively as we could, the FOXC1 - ARHGAP36 relationship. Our ChIP and RNA-seq datasets are freely available to other researchers via GEO (GSE297865/GSE297719). Our future manuscript is integrating ChIP-seq and RNA-seq with ATAC-seq: replicate ATAC-seq experiments permit rigorous characterization of genes transcriptionally regulated by Foxc1 as well as Foxc1’s pioneering abilities. However, these additional assays, and particularly validation of findings, take significant time and so lie beyond the scope of the current manuscript.

(3) RNA-seq and ChIP-seq data strongly suggest that FOXC1 regulates ARHGAP36 expression, and the authors convincingly identify genomic segments at the ARHGAP36 locus where FOXC1 binds, but they do not test if FOXC1 specifically activates this locus through the creation of a luciferase or similar promoter reporter. Such a reagent and associated experiments would not only strengthen the primary argument of this investigation but could serve as a valuable resource for the community of scientists investigating FOXC1, ARHGAP36, the Hedgehog pathway, and related biological processes. CRISPRi targeting of the identified regions of the ARHGAP locus is a useful step in the right direction, but these experiments are not done in a way to demonstrate FOXC1 dependency.

We agree and undertook the suggested luciferase reporter assays. The results demonstrate that transcriptional activity is dependent on Foxc1 and abrogated by mutation of the predicted Foxc1binding motifs (Fig. S8).

(4) It would be useful to see individual fluorescence channels in association with images in Figure 3b.

The figure has been revised to provide individual fluorescence channel data, as suggested.

(5) Perhaps the most significant limitation of this study is the omission of in vivo data, a shortcoming the authors partly mitigate through the incorporation of clinical outcome data from pediatric neuroblastoma patients in the context of ARHGAP36 expression. The authors also mention that high levels of ARHGAP36 expression were also detected in "specific CNS, breast, lung, and neuroendocrine tumors," but do not provide clinical outcome data for these cohorts. Such analyses would be useful to understand the generalizability of their findings across different cancer types. More broadly, how were high, medium, and low levels of ARHGAP36 expression identified? "Terciles" are mentioned, but such an approach is not experimentally rigorous, and RPA or related approaches (nested rank statistics, etc) are recommended to find optimal cutpoints for ARHGAP36 expression in the context of neuroblastoma, "specific CNS, breast, lung, and neuroendocrine" tumor outcomes.

The issue of analyzing in vivo data for neuroblastoma is addressed in more detail below, as it is also raised by the other reviewers. The neuroblastoma data represent the initial findings after the Foxc1Arhgap36 link was defined. There is vastly more that could and should be undertaken to determine mechanism(s) for ARHGAP36’s beneficial association with this tumor’ survival. This is the ongoing focus for the lab.

The original text omitted details of the cancer expression datasets surveyed that revealed high levels of ARHGAP36 expression were also detected in "specific CNS, breast, lung, and neuroendocrine tumors". This oversight has been corrected – when submitting, we omitted to upload a supplemental file (Table S4) that provided these data, which were derived from the following four sites (TCGA, TARGET, PCAWG and CCLE). However, these excellent online resources infrequently provide clinical outcome data.

The three independent neuroblastoma cohorts were analyzed identically. Each was stratified into an ordered dataset for ARHGAP36 expression, and then divided into three equal-sized groups [terciles]. Stratification into smaller subgroups [quartiles/quintiles] would have been equally feasible. The same methodology is used by the UCSC Xena browser for Kaplan-Meier survival analysis, and offers the advantage of avoiding a priori assumptions; it is thus agnostic regarding the data. We agree that there is scope for additional approaches, including recursive partitioning analyses, but suggest it may be better to reserve these for the future, not least in analyses that test the reported ARHGAP36-survival association in additional neuroblastoma datasets.

Reviewer #2 (Public review):

FOXC1 is a transcription factor essential for the development of neural crest-derived tissues and has been identified as a key biomarker in various cancers. … Together, these findings uncover a novel FOXC1-ARHGAP36 regulatory axis that modulates Hh and PKA signaling, offering new insights into both normal development and cancer progression.

The main strengths of the study are:

(1) Identification of a novel signaling pathway involving FOXC1 and ARHGAP36, which may play a critical role in both normal development and cancer biology.

(2) Mechanistic investigation using RNA-seq, ChIP-seq, and functional assays to elucidate how FOXC1 regulates ARHGAP36 and how this axis modulates Hh signaling.

(3) Clinical relevance demonstrated through analysis of neuroblastoma patient datasets, linking ARHGAP36 expression to improved 5-year overall survival.

The main weaknesses of the study are:

(1) Lack of validation in neuroblastoma models - the study does not directly test its findings in neuroblastoma cell models, limiting translational relevance.

We agree that the mechanisms by which increased ARHGAP36 levels are protective, are important to define. Despite experiments over many months manipulating ARHGAP36 expression, that induce quite rapid death of neuroblastoma cells in vitro, the precise mechanism(s) remain unresolved. Currently, we are endogenously labelling multiple neuroblastoma lines with Histone 2B-mCherry to facilitate live cell imaging and differentiate effects on proliferation and apoptosis. In the interim, we believe publication of the current dataset allows other researchers to independently test our findings for this pediatric malignancy. We are also establishing collaborations to access patient tissue samples, that will facilitate investigation of non cell autonomous mechanisms mediated via the tumor microenvironment.

(2) Incomplete mechanistic insight into PKA regulation - the study does not fully elucidate how FOXC1-ARHGAP36 regulates PKAC activity at the molecular level.

Other laboratories elegantly demonstrated that ARHGAP36’s effect on Hedgehog output is mediated by one motif blocking PKAC activity and the targeting of PKAC for degradation [PMIDs 25024229, 27713425, 30598432]. With these effects well-established, we limited experiments to confirming that Foxc1induced Arhgap36 reduced PKAC, and pT197 PKAC levels, to those of ectopic Arhgap36 expression.

(3) Insufficient discussion of clinical outcome data - while ARHGAP36 expression correlates with improved survival in neuroblastoma, the manuscript lacks a clear interpretation of this unexpected finding, especially given the known oncogenic roles of FOXC1, ARHGAP36, and Hh signaling.

ARHGAP36 expression may influence neuroblastoma survival via multiple mechanisms. Considering just canonical Hedgehog, possibilities include: cell cycle modulation, symmetric vs asymmetric cell division, maintenance of cancer stem cells, EMT, metastasis… Others include Hedgehog’s anti-apoptotic roles and the diverse mechanisms by which PKA influences cell function and survival. Faced with such diversity, we focused the discussion on what the presented data demonstrate.

Reviewer #3 (Public review):

Summary:

The focus of the research is to understand how transcription factors with high expression in neural crest cell-derived cancers (e.g., neuroblastoma) and roles in neural crest cell development function to promote malignancy. The focus is on the transcription factor FOXC1 and using murine cell culture, gain- and loss-of-function approaches, and ChIP profiling, among other techniques, to place PKC inhibitor ARHGAP36 mechanistically between FOXC1 and another pathway associated with malignancy, Sonic Hedgehog (SHH).

Strengths:

Major strengths are the mechanistic approaches to identify FOXC1 direct targets, definitively showing that FOXC1 transcriptional regulation of ARHGAP36 leads to dysregulation of SHH signaling downstream of ARHGAP36 inhibition of PKC. Starting from a screen of Foxc1 OE to get to ARHGAP36 and then using genetic and pharmacological manipulation to work through the mechanism is very well done. There is data that will be of use to others studying FOXC1 in mesenchymal cell types, in particular, the FOXC1 ChIP-seq.

Weaknesses:

Work is almost all performed in NIH3T3 or similar cells (mouse cells, not patient or mouse-derived cancer cells), so the link to neuroblastoma that forms the major motivation of the work is not clear. The authors look at ARHGAP36 levels in association with the neuroblastoma patient survival; however, the finding, though interesting and quite compelling, is misaligned with what the literature shows about FOXC1 and SHH, their high expression is associated with increased malignancy (also maybe worse outcomes?). Therefore, ARHGAP36 expression may be more complicated in a tumor cell or may be unrelated to FOXC1 or SHH, leaving one to wonder what the work in NIH3T3 cells, though well done, is telling us about the mechanisms of FOXC1 as an oncogene in neuroblastoma cells or in any type of cancer cell. Does it really function as an SHH activator to drive tumor growth? The 'oncogenic relevance' and 'contribution to malignancy' claimed in the last paragraph of the introduction are currently weakly supported by the data as presented. This could be improved by studying some of these mechanisms in patient-derived neuroblastoma cells with high FOXC1 expression. Does inhibiting FOXC1 change SHH and ARHGAP36 and have any effect on cell proliferation or migration? Alternatively, does OE of FOXC1 in NIH3T3 cells increase their migration or stimulate proliferation in some way, and is this dependent on ARHGAP36 or SHH? Application of their mechanistic approaches in cancer cells or looking for hallmarks of cancer phenotypes with FOXC1 OE (and dependent on SHH or ARHGAP36) could help to make a link with cellular phenotypes of malignant cells.

The manuscript stems from the lab’s findings that Foxc1 influences cilia-mediated signaling (Hedgehog and PDGFRalpha), offering an explanation for FOXC1’s pleiotropic phenotypes. Due to FOXC1’s largely unexplained roles in malignancy, the effects on Hedgehog prompted investigation of differential gene expression in NIH3T3 cells when Foxc1 was over-expressed. This identified Arhgap36 as a prime candidate for the Hedgehog pathway alterations, and most of the paper reports the characterization of this relationship. The final, small component of the paper, tests the relevance in neural crest derived cells, where Foxc1 has key roles. Neuroblastoma’s frequent lethality has created a network of highly supportive researchers with shared datasets, and these survival data were assayed. This in turn revealed that high levels of ARHGAP36 expression were associated with a favorable survival outcome.

Defining the underlying molecular mechanisms for this novel association is clearly important. As outlined above, one challenge reflects the diversity of potential mechanisms, coupled with the requirement to validate those identified from 2-D culture in patient-derived tumor explants as well as immuno-deficient model organisms. Such experiments take significant time, and our present focus is on manipulating ARHGAP36 expression directly, rather than by altering FOXC1 expression, which inevitably has even more diverse effects.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The study would be strengthened by validating key findings, such as the resistance to Hh inhibition, in neuroblastoma cell lines to enhance disease relevance.

Planned future experiments include in vitro evaluation of PKA antagonists and agonists on neuroblastoma survival.

The authors show that FOXC1/ARHGAP36 reduces PKAC protein levels; however, it is unclear whether this regulation occurs at the transcriptional level. Assessing PKAC mRNA expression would help explain the mechanism. Additionally, if PKAC is transcriptionally downregulated, overexpression of PKAC can be used to test whether it reverses the FOXC1/ARHGAP36induced activation of Hh signaling.

The RNA-sequencing data exclude this possibility at the transcriptional level, since PKA is not significantly differentially expressed (Table S1). Instead, Figures 1&3 support Foxc1 inducing Arhgap36 expression, with elevated Arhgap36 protein levels reducing those of PKAC and catalytically active pT197 PKAC, in both the cytoplasm and adjacent to the basal body.

The Discussion should address the potential effects of ARHGAP36 overexpression on other signaling pathways-particularly Hh and PKA signaling and PKA in neuroblastoma. These effects may help interpret the observed association between ARHGAP36 expression and clinical outcomes in patients. Of note, it has been reported that Hh may correlate with better survival in neuroblastoma (Cancers, 2021 Apr 15;13(8):1908; J Pediatr Surg. 2010 Dec;45(12):2299).

Both Hedgehog signaling and protein kinase A have broad effects on normal cell biology, that are likely more extensive in malignant cells. Consequently, although tempting to propose why ARHAGP36 overexpression is associated with enhanced survival, it may be better to wait until the causative mechanisms have been defined.

If treatment information for the patient cohorts is available, it should be included as it may enhance the interpretability of the survival analyses.

This is an excellent suggestion, although at present this information is not available to us. As the manuscript moves forward to publication, we will be liaising with the corresponding authors of the three datasets [GSE49711, E-MTAB-178191 and TARGET] to explore such additional clinical possibilities.

The 'A' label in Figures S9 and S10 should be removed, as neither figure contains sub-panels.

This has been corrected, as suggested.

Reviewer #3 (Recommendations for the authors):

Other comments:

(1) Figure 5A, B: Unclear how meaningful the inhibitor experiments are in the absence of SHH (presumable none in the media or made by NIH3T3 cells?), other than as a control for the FOXC1 OE treated with Smo antagonists. A potentially better experiment could be to take malignant cells with high FOXC1 and high SHH signaling and put on Smo inhibitors.

Figure 5A demonstrates Foxc1’s induction of GLI1 expression is not dependent on Hedgehog ligand. While certainly feasible to repeat in malignant cells strongly expressing FOXC1, doing this comprehensively would require testing lines from many or all of the ~15 malignancies where FOXC1 has a defined contribution.

(2) Figure 6: the Gli2-mGFP seem to have higher levels of ciliary Sufu, they also have higher levels of Gli1 (see Figure 1C), does the Gli2-mGFP expression change SHH signaling? What controls have the authors done to test if this is a serious confound in their studies? They use it for most experiments, this is important to address.

Although Gli2-mGFP expression affects Hedgehog signaling, in the absence of Gli2 (e.g. untransformed NIH3T3) Foxc1 induces Arhgap36 expression. The scope for interaction between Foxc1 and Gli2 represents an additional motivation for the ATAC-seq experiments described above to better determine if these two transcription factors have synergistic effects.

(3) Figure 3B: (1) Please use color-blind friendly LUTs for the signals (same comment for other figures), (2) The Gli2-mGFP line with the current color scheme is confusing; it looks like only 647 and 555 secondaries were used, did they not image with the mGFP? Why not? (3) What is the evidence that these are basal bodies? (4) Why did the authors use cycloheximide in these IF experiments? Was this also done in other methods? The reasoning behind this is missing.

For now, we have included separate channels for Figure 3. In future manuscripts we will adopt the suggestion of moving to either magenta and green, or cyan and magenta combinations for depicting immunofluorescence.

eLife Assessment

This valuable study utilizes a newly developed approach to culture T gondii bradyzoites in myotubes, and then takes advantage of the antiparasitic compound collection known as the Pathogen Box, to find compounds that target both tachyzoite and bradyzoite forms of the parasite. A set of compounds yielding patterns consistent with targeting the mitochondrial bc1 complex was explored further, with convincing evidence for changes in ATP production in bradyzoites to support the conclusions about the importance of this complex. The paper will be interesting for parasitologists studying drug discovery of apicomplexan parasites.

Reviewer #1 (Public review):

Summary:

The authors' goal was to advance the understanding of metabolic flux in the bradyzoite cyst form of the parasite T. gondii, since this is a major form of transmission of this ubiquitous parasite, but very little is understood about cyst metabolism and growth. This is an important advance in understanding and targeting bradyzoite growth.

Strengths:

The study used a newly developed technique for growing T. gondii cystic parasites in a human muscle-cell myotube format, which enables culturing and analysis of cysts. This enabled screening of a set of anti-parasitic compounds to identify those that inhibit growth in both vegetative (tachyzoite) forms and bradyzoites (cysts). Three of these compounds were used for comparative Metabolomic profiling to demonstrate differences in metabolism between the two cellular forms.<br /> One of the compounds yielded a pattern consistent with targeting the mitochondrial bc1 complex, and suggest a role for this complex in metabolism in the bradyzoite form, an important advance in understanding this life stage.

Weaknesses:

Studies such as these provide important insights into the overall metabolic differences between different life stages, and they also underscore the challenge with interpreting individual patterns caused by metabolic inhibitors due to the systemic level of some of the targets. The authors have employed mock treatment and non-metabolic inhibitor controls to alleviate these challenges.

Reviewer #2 (Public review):

Summary:

A particular challenge in treating infections caused by the parasite Toxoplasma gondii is to target (and ultimately clear) the tissue cysts that persist for the lifetime of an infected individual. The study by Maus and colleagues leverages the development of a powerful in vitro culture system for the cyst-forming bradyzoite stage of Toxoplasma parasites to screen a compound library for candidate inhibitors of parasite proliferation and survival. They identify numerous inhibitors capable of inhibiting both the disease-causing tachyzoite and the cyst-forming bradyzoite stages of the parasite. To characterize the potential targets of some of these inhibitors, they undertake metabolomic analyses. The metabolic signatures from these analyses lead them to identify one compound (MMV1028806) that interferes with aspects of parasite mitochondrial metabolism. In the revised version of the manuscript, the authors present convincing evidence that MMV1028806 targets the mitochondrial electron transport (ETC) chain of the parasite (although they don't identify the actual target in the ETC). The revised manuscript also nicely addresses my other criticisms of the original version. Overall, the study presents an exciting approach for identifying and characterizing much-needed inhibitors for targeting tissue cysts in these parasites.

Strengths:

The study presents convincing proof-of-principle evidence that the myotube-based in vitro culture system for T. gondii bradyzoites can be used to screen compound libraries, enabling the identification of compounds that target the proliferation and/or survival of this stage of the parasite. The study also utilizes metabolomic approaches to characterize metabolic 'signatures' that provide clues to the potential targets of candidate inhibitors. In addition to insights into candidate bradyzoite inhibitors, the study also provides new insights into the physiological role of the mitochondrial electron transport chain of bradyzoites, and raises a host of interesting questions around the functional roles of mitochondria in this stage of the parasite.

Weaknesses:

As noted in my previous review, the authors present convincing evidence that one of the compounds they have identified (MMV1028806) is targeting the mitochondrial electron transport chain (ETC). However, in the absence of an assay that directly measures bc1 activity (e.g. an enzymatic assay), they cannot be certain that it targets the bc1 complex in the ETC. I appreciate that the authors have toned down some of the conclusions around this. I do still think there are some places where the text is overstating the finding (noted below).

Line 30. "Stable isotope-resolved metabolic profiling on tachyzoites and bradyzoites identified the mitochondrial bc1-complex as a target of bradyzocidal compounds".

Line 546. "Metabolic profiling and stable isotope tracing in treated tachyzoites suggested the inhibition of the mitochondrial bc1-complex by MMV1028806 and the reference compound BPQ."

Line 622. "In addition to abundance data, the incorporation of ¹³C and ¹⁵N stable isotopes from glucose and glutamine, respectively, into TCA cycle and pyrimidine biosynthesis intermediates suggest the bc1-complex as a target."

Reviewer #3 (Public review):

Summary:

The authors described an exciting 400-drug screening using a MMV pathogen box to select compounds that effectively affects the medically important Toxoplasma parasite bradyzoite stage. This work utilises a bradyzoites culture technique that was published recently by the same group. They focused on compounds that affected directly the mitochondria electron transport chain (mETC) bc1-complex and compared with other bc1 inhibitors described in the literature such as atovaquone and HDQs. They further provide metabolomics analysis of inhibited parasites which serves to provide support for the target and to characterise the outcome of the different inhibitors.

Strengths:

This work is important as, until now, there are no effective drugs that clear cysts during T. gondii infection. So, the discovery of new inhibitors that are effective against this parasite-stage in culture and thus have the potential to battle chronic infection is needed. The further metabolic characterization provides indirect target validation and highlight different metabolic outcome for different inhibitors. The latter forms the basis for new studied in the field to understand the mode of inhibition and mechanism of bc1-complex function in detail.

The authors focused in the function of one compound, MMV1028806, that is demonstrated to have a similar metabolic outcome to burvaquone. Furthermore, the authors evaluated the importance of ATP production in tachyzoite and bradyzoites stages and under atovaquone/HDQs drugs.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors' goal was to advance the understanding of metabolic flux in the bradyzoite cyst form of the parasite T. gondii, since this is a major form of transmission of this ubiquitous parasite, but very little is understood about cyst metabolism and growth.

Nonetheless, this is an important advance in understanding and targeting bradyzoite growth.

Strengths:

The study used a newly developed technique for growing T. gondii cystic parasites in a human muscle-cell myotube format, which enables culturing and analysis of cysts. This enabled screening of a set of anti-parasitic compounds to identify those that inhibit growth in both vegetative (tachyzoite) forms and bradyzoites (cysts). Three of these compounds were used for comparative Metabolomic profiling to demonstrate differences in metabolism between the two cellular forms.

One of the compounds yielded a pattern consistent with targeting the mitochondrial bc1 complex, and suggest a role for this complex in metabolism in the bradyzoite form, an important advance in understanding this life stage.

Weaknesses:

Studies such as these provide important insights into the overall metabolic differences between different life stages, and they also underscore the challenge with interpreting individual patterns caused by metabolic inhibitors due to the systemic level of some of some targets, so that some observed effects are indirect consequences of the inhibitor action. While the authors make a compelling argument for focusing on the role of the bc1 complex, there are some inconsistencies in the some patterns that underscore the complexity of metabolic systems.

Thank you for reviewing the revised manuscript.

Reviewer #2 (Public review):

Summary:

A particular challenge in treating infections caused by the parasite Toxoplasma gondii is to target (and ultimately clear) the tissue cysts that persist for the lifetime of an infected individual. The study by Maus and colleagues leverages the development of a powerful in vitro culture system for the cyst-forming bradyzoite stage of Toxoplasma parasites to screen a compound library for candidate inhibitors of parasite proliferation and survival. They identify numerous inhibitors capable of inhibiting both the disease-causing tachyzoite and the cyst-forming bradyzoite stages of the parasite. To characterize the potential targets of some of these inhibitors, they undertake metabolomic analyses. The metabolic signatures from these analyses lead them to identify one compound (MMV1028806) that interferes with aspects of parasite mitochondrial metabolism. In the revised version of the manuscript, the authors present convincing evidence that MMV1028806 targets the mitochondrial electron transport (ETC) chain of the parasite (although they don't identify the actual target in the ETC). The revised manuscript also nicely addresses my other criticisms of the original version. Overall, the study presents an exciting approach for identifying and characterizing much-needed inhibitors for targeting tissue cysts in these parasites.

Strengths:

The study presents convincing proof-of-principle evidence that the myotube-based in vitro culture system for T. gondii bradyzoites can be used to screen compound libraries, enabling the identification of compounds that target the proliferation and/or survival of this stage of the parasite. The study also utilizes metabolomic approaches to characterize metabolic 'signatures' that provide clues to the potential targets of candidate inhibitors. In addition to insights into candidate bradyzoite inhibitors, the study also provides new insights into the physiological role of the mitochondrial electron transport chain of bradyzoites, and raises a host of interesting questions around the functional roles of mitochondria in this stage of the parasite.

Weaknesses:

In the revised manuscript, the authors have included additional oxygen consumption rate data that indicate that MMV1028806 targets the mitochondrial electron transport chain (ETC). These data are convincing. On line 481, the authors state that "treatments with ATQ, BPQ, MMV1028806, and antimycin A resulted in substantially reduced oxygen consumption levels relative to the DMSO control and suggest indeed a blockage of the mETC consistent with the inhibition of the bc1-complex." The OCR assay the authors use is still only an indirect measure of bc1 activity. Given that most OCR-inhibiting compounds in T. gondii are bc1 inhibitors, it is possible (and perhaps likely) that MMV1028806 is targeting this complex. However, the data cannot rule out that it is targeting another component of the ETC (or potentially even a TCA cycle enzyme). Without a direct test that MMV1028806 inhibits bc1 complex activity, the authors should be more cautious in their interpretation (e.g. by acknowledging the limitations of their conclusion, or acknowledging other possible targets). Similarly, the conclusion on line Line 622 that "... we confirmed the bc1-complex as a target" is overstating the findings. The phrasing on lines 683-695 is more appropriate: "... suggesting that it also targets complex III or a functionally linked site within the mitochondrial electron transport chain."

We are grateful for he thorough review of the updated manuscript and the identification the minor issues. We addressed all of them as detailed below. We also tempered our conclusions regarding the identification of the bc1-complex as a target in line 616:

“In addition to abundance data, Additionally, we confirmed the bc1-complex as a target by monitoring the incorporation of ¹³C and ¹⁵N stable isotopes from glucose and glutamine, respectively, into TCA cycle and pyrimidine biosynthesis intermediates suggest the bc1-complex as a target”

Reviewer #3 (Public review):

Summary:

The authors described an exciting 400-drug screening using a MMV pathogen box to select compounds that effectively affect the medically important Toxoplasma parasite bradyzoite stage. This work utilises a bradyzoites culture technique that was published recently by the same group. They focused on compounds that affected directly the mitochondria electron transport chain (mETC) bc1-complex and compared with other bc1 inhibitors described in the literature such as atovaquone and HDQs. They further provide metabolomics analysis of inhibited parasites which serves to provide support for the target and to characterise the outcome of the different inhibitors.

Strengths:

This work is important as, until now, there are no effective drugs that clear cysts during T. gondii infection. So, the discovery of new inhibitors that are effective against this parasite-stage in culture and thus have the potential to battle chronic infection is needed. The further metabolic characterization provides indirect target validation and highlight different metabolic outcome for different inhibitors. The latter forms the basis for new studies in the field to understand the mode of inhibition and mechanism of bc1-complex function in detail.

The authors focused in the function of one compound, MMV1028806, that is demonstrated to have a similar metabolic outcome to burvaquone. Furthermore, the authors evaluated the importance of ATP production in tachyzoite and bradyzoites stages and under atovaquone/HDQs drugs.

Thank you for reviewing the revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Thanks for making appropriate updates. I believe it makes the report stronger. Just please double-check proof-reading in newly added text: for example "integration" is misspelled in Figure 4 legend (C, E).

Typos have been corrected throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

I congratulate the authors on an excellent study. I have several minor comments for the authors to consider before publication.

Line 99. Schistosoma –

Corrected

Line 123. What was the pH of the bicarb-free RPMI medium?

Added “at pH 7.2”

Line 218 (and again on line 687). "RHku80" - are these just standard RH strain parasites? Or do the authors mean to imply that the ku80 gene has been knocked out in this line? If the latter, RH∆ku80 may be a better way to describe this line.

We harmonized all mentions of this strain to RH∆ku80.

Line 225. "Parasites were incubated in medium with one of the following treatments ..." How long were the parasites incubated in the different treatments before the plate was read? Was there any preincubation? I think not, but it would help to state this so the reader can appreciate that the effects of the compounds on OCR is likely an immediate (rather than a secondary) effect.

This is indeed a good suggestion. There was no pre-incubation and we added changed the text to: “Parasites were incubated in medium with one of the following treatments immediately before measurement: … “

Figure S2A. Check the spelling of Toxoplasmosis.

Done, we corrected this sentence.

Figure S2B. do you mean 'tachyzoidal' or 'tachyzocidal'? 'bradyzoidal' or 'bradyzocidal'?

We clarified the formulation of the legends for Fig S2.

Figure S2D. The "Tachyzoite lowest cytotoxicity" and "Bradyzoite lowest cytotoxicity" columns are, I think, depicting compound toxicity in host cells. Would it be clearer to rename these columns relative to the host cells being tested? e.g. "HFF/KD3 myotube lowest cytotoxicity"

Good suggestion and we changed the designation accordingly.

Line 369. "We found that tachyzocidal, bradyzocidal and dually active compounds possess a statistically significantly higher lipophilicity and this trend appeared more accentuated for bradyzocidal and dually active compounds." Significantly higher than what? Need to be clearer about the comparison being made: i.e. to non-active compounds.

You are correct and we corrected this sentence accordingly.

Line 500. "we attribute these changes to inhibition of host mitochondria (Fig. 5A)." The reason for referencing Figure 5A here isn't clear. Do the authors mean to point out that host mitochondrial membrane potential is affected by compound treatment? This could be stated more clearly.

We deleted the reference to Fig 5A. We did not systematically measure the effect of the inhibitors on the membrane potential of the host mitochondria. We also changed the sentence to emphasize the speculative nature of this assertion: “we attribute these changes to potential inhibitory effects on host mitochondria”.

Line 840. 'hurdling mechanisms'. The authors don't explain what they mean by this expression.

We truncated the figure title to: “Untargeted metabolomic analysis of bradyzoites treated with bc1-complex inhibitors shows an energy imbalance.”

eLife assessment

This study presents an important finding of dynamic reprogramming of global H3K4me2 during mouse oocyte-to-embryo transition. While the H3K4me2 epigenome data is convincing, the interpretation and the potential mechanistic claims of the authors are incomplete in the current shape with the primary concerns regarding the contribution of Kdm1b or Kdm1a, as well as the specificity of the inhibitor and the antibody. The work will be of interest to researchers interested in epigenetic reprogramming.

Reviewer #1 (Public Review):

By mapping H3K4me2 in mouse oocytes and pre-implantation embryos, the authors aim to elucidate how this histone modification is erased and re-established during the parental-to-zygotic transition, as well as how the reprogramming of H3K4me2 regulates gene expression and facilitates zygotic genome activation.

Employing an improved CUT&RUN approach, the authors successfully generated H3K4me2 profiling data from a limited number of embryos. While the profiling experiments are very well executed, several weaknesses, particularly in data analysis, are apparent:

(1) The study emphasizes H3K4me2, which often serves as a precursor to H3K4me3, a well-studied modification during early development. Analyzing the new H3K4me2 dataset alongside published H3K4me3 data is crucial for comprehensively understanding epigenetic reprogramming post-fertilization and the interplay between histone modifications. However, the current analysis is preliminary and lacks depth.

(2) Tranylcypromine (TCP) is known as an irreversible inhibitor of monoamine oxidase and LSD1. While the authors suggest TCP inhibits the expression of LSD2, this assertion is questionable. Given TCP's potential non-specific effects in cells, conclusions related to the experiments using TCP should be made with caution.

(3) Some batches of H3K4me2 antibody are known to cross-react with H3K4me3. Has the H3K4me2 antibody used in CUT&RUN been tested for such cross-reactivity? Heatmaps in the figures indeed show similar distribution for H3K4me2 and H3K4me3, further raising concerns about antibody specificity.

(4) Certain statements lack supporting references or figures (examples on page 9 can be found on line 245, line 254, and line 258).

(5) Extensive language editing is recommended to clarify ambiguous sentences. Additionally, caution should be taken to avoid overstatement - most analyses in this study only suggest correlation rather than causality.

Reviewer #2 (Public Review):

Chong Wang et al. investigated the role of H3K4me2 during the reprogramming processes in mouse preimplantation embryos. The authors show that H3K4me2 is erased from GV to MII oocytes and re-established in the late 2-cell stage by performing Cut & Run H3K4me2 and immunofluorescence staining. Erasure and re-establishment of H3K4me2 have not been studied well, and profiling of H3K4me2 in germ cells and preimplantation embryos is valuable to understanding the reprogramming process and epigenetic inheritance.

(1) The authors claim that the Cut & Run worked for MII oocytes, zygotes, and the 2-cell embryos. However, it is unclear if H3K4me2 is erased during the stage or if the Cut & Run did not work for these samples. To support the hypothesis of the erasure of H3K4me2, the authors conducted immunofluorescence staining, and H3k4me2 was undetected in the MII oocyte, PN5, and 2-cell stage. However, the published papers showed strong staining of H3K4me2 at the zygote stage and 2-cell stage ((Ancelin et al., 2016; Shao et al., 2014)). The authors need to cite these papers and discuss the contradictory findings.

The authors used 165 MII oocytes and 190 GV oocytes for the Cut & Run. The amount of DNA in MII oocytes is halved because of the emission of the first polar body. Would it be a reason that H3K4me2 has fewer H3K4me2 peaks in MII oocytes than GV oocytes?

In Figure 3C, 98% (13,183/13,428) of H3K4me2 marked genes in GV oocytes overlap with those in the 4-cell stage. Furthermore, 92% (14,049/15,112) of H3K4me2 marked genes in sperm overlap with those in the 4-cell stage. Therefore, most regions maintain germ line-derived H3K4me2 in the 4-cell stage. The authors need to clarify which regions of germ line-derived H3K4me2 are maintained or erased in preimplantation embryos. Additionally, it would be interesting to investigate which regions show the parental allele-specific H3K4me2 in preimplantation embryos since the authors used hybrid preimplantation embryos (B6 x DBA).

(2) The authors claim that Kdm1a is rarely expressed during mouse embryonic development (Figure 4A). However, the published paper showed that KDM1a is present in the zygote and 2-cell stage using immunostaining and western blotting ((Ancelin et al., 2016)). Additionally, this paper showed that depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage, and therefore, KDM1a is functionally important in early development. The authors should have cited the paper and described the role of KDM1a in early embryos.

(3) The authors used the published RNA data set and interpreted that KDM1B (LSD2) was highly expressed at the MII stage (Figure S3A). However, the heat map shows that KDM1B expression is high in growing oocytes but not at 8w_oocytes and MII oocytes. The authors need to interpret the data accurately.

(4) All embryos in the TCP group were arrested at the four-cell stage. Embryos generated from KDM1b KO females can survive until E10.5 (Ciccone et al., 2009); therefore, TCP-treated embryos show a more severe phenotype than oocyte-derived KDM1b deleted embryos. Depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage ((Ancelin et al., 2016)). The authors need to examine whether TCP treatment affects KDM1a expression. Western blotting would be recommended to quantify the expression of KDM1A and KDM1B in the TCP-treated embryos.

(5) H3K4me2 is increased dramatically in the TCP-treated embryos in Figure 4 (the intensity is 1,000 times more than the control). However, the Cut & Run H3K4me2 shows that the H3K4me2 signal is increased in 251 genes and decreased in 194 genes in the TCP-treated embryos (Fold changes > 2, P < 0.01). The authors need to explain why the gain of H3K4me2 is less evident in the Cut & Run data set than in the immunofluorescence result.

References

Ancelin, K., ne Syx, L., Borensztein, M., mie Ranisavljevic, N., Vassilev, I., Briseñ o-Roa, L., Liu, T., Metzger, E., Servant, N., Barillot, E., Chen, C.-J., Schü le, R., & Heard, E. (2016). Maternal LSD1/KDM1A is an essential regulator of chromatin and transcription landscapes during zygotic genome activation. https://doi.org/10.7554/eLife.08851.001

Ciccone, D. N., Su, H., Hevi, S., Gay, F., Lei, H., Bajko, J., Xu, G., Li, E., & Chen, T. (2009). KDM1B is a histone H3K4 demethylase required to establish maternal genomic imprints. Nature, 461(7262), 415-418. https://doi.org/10.1038/nature08315

Shao, G. B., Chen, J. C., Zhang, L. P., Huang, P., Lu, H. Y., Jin, J., Gong, A. H., & Sang, J. R. (2014). Dynamic patterns of histone H3 lysine 4 methyltransferases and demethylases during mouse preimplantation development. In Vitro Cellular and Developmental Biology - Animal, 50(7), 603-613. https://doi.org/10.1007/s11626-014-9741-6

Reviewer #3 (Public Review):

Summary:

This study explores the dynamic reprogramming of histone modification H3K4me2 during the early stages of mammalian embryogenesis. Utilizing the advanced CUT&RUN technique coupled with high-throughput sequencing, the authors investigate the erasure and re-establishment of H3K4me2 in mouse germinal vesicle (GV) oocytes, metaphase II (MII) oocytes, and early embryos.

Strengths:

The findings provide valuable insights into the temporal and spatial dynamics of H3K4me2 and its potential role in zygotic genome activation (ZGA).

Weaknesses:

The study primarily remains descriptive at this point. It would be advantageous to conduct further comprehensive functional validation and mechanistic exploration.<br /> Key areas for improvement include enhancing the innovation and novelty of the study, providing robust functional validation, establishing a clear model for H3K4me2's role, and addressing technical and presentation issues. The text would benefit from the introduction of a novel conceptual framework or model that provides a clear explanation of the functional consequences and molecular mechanisms underlying H3K4me2 reprogramming in the transition from parental to early embryonic development.

While the findings are significant, the current manuscript falls short in several critical areas. Addressing major and minor issues will significantly strengthen the study's contribution to the field of epigenetic reprogramming and embryonic development.

Author response:

Public Reviews:

Reviewer #1 (Public Review):

By mapping H3K4me2 in mouse oocytes and pre-implantation embryos, the authors aim to elucidate how this histone modification is erased and re-established during the parental-to-zygotic transition, as well as how the reprogramming of H3K4me2 regulates gene expression and facilitates zygotic genome activation.

Employing an improved CUT&RUN approach, the authors successfully generated H3K4me2 profiling data from a limited number of embryos. While the profiling experiments are very well executed, several weaknesses, particularly in data analysis, are apparent:

(1) The study emphasizes H3K4me2, which often serves as a precursor to H3K4me3, a well-studied modification during early development. Analyzing the new H3K4me2 dataset alongside published H3K4me3 data is crucial for comprehensively understanding epigenetic reprogramming post-fertilization and the interplay between histone modifications. However, the current analysis is preliminary and lacks depth.

Thank you very much for your valuable suggestions. The data of histone H3K4me3 in humans and mice has been published，and our previous data revealed the unique pattern of H3K4me3 during early human embryos and oocytes (Science. 2019 Jul 26;365(6451):353-360.) . So, this study mainly focuses on the localization of H3K4me2 in mouse oocytes and preimplantation embryos, how it is erased and re-established during mammalian parental-to-zygote transition, and its function. The combined analysis of H3K4me2 and H3K4me3 is not our main work, but it is not ruled out that there may be new discoveries between these two histones. Previously, our data tended to show that the H3K4me2 not only acts as a precursor of H3K4me3, but also plays its role independently.

(2) Tranylcypromine (TCP) is known as an irreversible inhibitor of monoamine oxidase and LSD1. While the authors suggest TCP inhibits the expression of LSD2, this assertion is questionable. Given TCP's potential non-specific effects in cells, conclusions related to the experiments using TCP should be made with caution.

Thank you for pointing this out, and we thank the reviewer again for the important suggestion. We found that the previous study (.Binda C, Valente S, Romanenghi M, Pilotto S, Cirilli R, Karytinos A, Ciossani G, Botrugno OA, Forneris F, Tardugno M, Edmondson DE, Minucci S, Mattevi A, Mai A. Biochemical, structural, and biological evaluation of tranylcypromine derivatives as inhibitors of histone demethylases LSD1 and LSD2. J Am Chem Soc. 2010 May 19;132(19):6827-33.) indicated that TCP was a non-reversible inhibitor of LSD1 and LSD2 (Human LSD2/KDM1b/AOF1 Regulates Gene Transcription by Modulating Intragenic H3K4me2 Methylation, Mol Cell. 2010 Jul 30; 39(2): 222–233.), but according to our data, the content of LSD1 was very low in the early stages of mouse embryos, which mainly inhibited the function of LSD2.

(3) Some batches of H3K4me2 antibody are known to cross-react with H3K4me3. Has the H3K4me2 antibody used in CUT&RUN been tested for such cross-reactivity? Heatmaps in the figures indeed show similar distribution for H3K4me2 and H3K4me3, further raising concerns about antibody specificity.

We thank the reviewer for the insightful comments. The H3K4me2 antibody was purchased from Millipore (cat. 07030). Figure 2A shows the specific enrichment area of H3K4me2 in promoter and distal region. Some batches of H3K4me2 antibody are known to cross-react with H3K4me3, but the H3K4me2 antibody we used in our CUT&RUN seems to have Low cross-reactivity.

(4) Certain statements lack supporting references or figures (examples on page 9 can be found on line 245, line 254, and line 258).

Thank you for pointing this out, and we will add references to support the statement in the paper as suggested.

(5) Extensive language editing is recommended to clarify ambiguous sentences. Additionally, caution should be taken to avoid overstatement - most analyses in this study only suggest correlation rather than causality.

Thank you for your kind comments. We will revise the expression in the manuscript later.

Reviewer #2 (Public Review):

Chong Wang et al. investigated the role of H3K4me2 during the reprogramming processes in mouse preimplantation embryos. The authors show that H3K4me2 is erased from GV to MII oocytes and re-established in the late 2-cell stage by performing Cut & Run H3K4me2 and immunofluorescence staining. Erasure and re-establishment of H3K4me2 have not been studied well, and profiling of H3K4me2 in germ cells and preimplantation embryos is valuable to understanding the reprogramming process and epigenetic inheritance.

(1) The authors claim that the Cut & Run worked for MII oocytes, zygotes, and the 2-cell embryos. However, it is unclear if H3K4me2 is erased during the stage or if the Cut & Run did not work for these samples. To support the hypothesis of the erasure of H3K4me2, the authors conducted immunofluorescence staining, and H3k4me2 was undetected in the MII oocyte, PN5, and 2-cell stage. However, the published papers showed strong staining of H3K4me2 at the zygote stage and 2-cell stage ((Ancelin et al., 2016; Shao et al., 2014)). The authors need to cite these papers and discuss the contradictory findings.

The authors used 165 MII oocytes and 190 GV oocytes for the Cut & Run. The amount of DNA in MII oocytes is halved because of the emission of the first polar body. Would it be a reason that H3K4me2 has fewer H3K4me2 peaks in MII oocytes than GV oocytes?

First of all, thank you for your valuable advice. The published papers showed strong staining of H3K4me2 at the zygote stage and 2-cell stage (Ancelin et al., 2016), which is interesting. I think we may have used different parameters in the confocal laser shooting process. We used the same parameter to continuously shoot the blastocyst stage from the GV stage. If we only shot the fertilized egg and the 2-cell stage, I think we may also see weak fluorescence at the 2-cell stage under different parameters. We will refer to this reference and discuss it in the resubmitted version.

Moreover, you mentioned the H3K4me2 has fewer H3K4me2 peaks in MII oocytes than GV oocytes, because the MII expelled the polar body. There is no problem with this logic. However, the first polar body expelled from the MII stage is still in the zona pellucida, and we also collected the polar body in the CUT&RUN experiment; Therefore, compared to GV, the DNA content of MII samples is not halved. After further discussion, we believe that the reduction of H3K4me2 peaks in MII stage compared with GV stage may be closely related to oocyte maturation. It is the specific modification of histones in different forms at different times that affects the chromatin structure change appropriately with the different stages of meiosis. At present, it has been confirmed that H3K4me3 gradually decreases from GV to MII stage during the maturation of human oocytes. H3K27me3 did not change from GV to MII stage.

In Figure 3C, 98% (13,183/13,428) of H3K4me2 marked genes in GV oocytes overlap with those in the 4-cell stage. Furthermore, 92% (14,049/15,112) of H3K4me2 marked genes in sperm overlap with those in the 4-cell stage. Therefore, most regions maintain germ line-derived H3K4me2 in the 4-cell stage. The authors need to clarify which regions of germ line-derived H3K4me2 are maintained or erased in preimplantation embryos. Additionally, it would be interesting to investigate which regions show the parental allele-specific H3K4me2 in preimplantation embryos since the authors used hybrid preimplantation embryos (B6 x DBA).

Thank you very much for your suggestion. Further analysis of which regions show the parental allele-specific H3K4me2 in preimplantation embryos will make the study more interesting. We will discuss this in depth in resubmitted vision.

(2) The authors claim that Kdm1a is rarely expressed during mouse embryonic development (Figure 4A). However, the published paper showed that KDM1a is present in the zygote and 2-cell stage using immunostaining and western blotting (Ancelin et al., 2016). Additionally, this paper showed that depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage, and therefore, KDM1a is functionally important in early development.

The authors should have cited the paper and described the role of KDM1a in early embryos.

In the analysis of this experiment, we believe that in the early embryonic development of mice, the expression of KDM1A is lower than that of KDM1B, which is relative. Similarly, the transcriptome data we cite also show that KDM1A is expressed at elevated levels during oocyte maturation and fertilization compared to immature oocytes. In addition, the effects of loss of maternal KDM1a on embryonic development were not discussed. We believe that the absence of maternal KDM1b blocks embryonic development, and we will cite and discus the references later.

(3) The authors used the published RNA data set and interpreted that KDM1B (LSD2) was highly expressed at the MII stage (Figure S3A). However, the heat map shows that KDM1B expression is high in growing oocytes but not at 8w_oocytes and MII oocytes. The authors need to interpret the data accurately.

After re-checking the data, we found that there was a problem with the normalization method of our heat map, and we will re-make the heatmap and submit it in the modified version. With reference to Figure 4A, the content of Kdm1b is indeed higher than that of Kdm1a.

(4) All embryos in the TCP group were arrested at the four-cell stage. Embryos generated from KDM1b KO females can survive until E10.5 (Ciccone et al., 2009); therefore, TCP-treated embryos show a more severe phenotype than oocyte-derived KDM1b deleted embryos. Depletion of maternal KDM1A protein results in developmental arrest at the two-cell stage ((Ancelin et al., 2016)). The authors need to examine whether TCP treatment affects KDM1a expression. Western blotting would be recommended to quantify the expression of KDM1A and KDM1B in the TCP-treated embryos.

We will further dig the transcriptome data to confirm the specificity of TCP to KDM1b. In addition, the intervention of TCP on the whole fertilized egg in this study increased the H3K4me2 content, and the embryo development retarding effect was more significant than that obtained by crossing with normal paternal lines after knocking down KDM1B from the mother.

(5) H3K4me2 is increased dramatically in the TCP-treated embryos in Figure 4 (the intensity is 1,000 times more than the control). However, the Cut & Run H3K4me2 shows that the H3K4me2 signal is increased in 251 genes and decreased in 194 genes in the TCP-treated embryos (Fold changes > 2, P < 0.01). The authors need to explain why the gain of H3K4me2 is less evident in the Cut & Run data set than in the immunofluorescence result.

Thanks a lot for your question. In the experimental group, the fluorescence value of H3K4me2 in IF was increased by 1000 times (Figure 4E), and the expression of H3K4Me2-related genes in CR was up-regulated and down-regulated for a total of 445 changes (Figure 6A). In our opinion, as a semi-quantitative analysis, immunofluorescence cannot be compared with the quantitative analysis method of CR because of the different analysis models and threshold Settings.

References

Ancelin, K., ne Syx, L., Borensztein, M., mie Ranisavljevic, N., Vassilev, I., Briseñ o-Roa, L., Liu, T., Metzger, E., Servant, N., Barillot, E., Chen, C.-J., Schü le, R., & Heard, E. (2016). Maternal LSD1/KDM1A is an essential regulator of chromatin and transcription landscapes during zygotic genome activation. https://doi.org/10.7554/eLife.08851.001

Ciccone, D. N., Su, H., Hevi, S., Gay, F., Lei, H., Bajko, J., Xu, G., Li, E., & Chen, T. (2009). KDM1B is a histone H3K4 demethylase required to establish maternal genomic imprints. Nature, 461(7262), 415-418. https://doi.org/10.1038/nature08315

Shao, G. B., Chen, J. C., Zhang, L. P., Huang, P., Lu, H. Y., Jin, J., Gong, A. H., & Sang, J. R. (2014). Dynamic patterns of histone H3 lysine 4 methyltransferases and demethylases during mouse preimplantation development. In Vitro Cellular and Developmental Biology - Animal, 50(7), 603-613. https://doi.org/10.1007/s11626-014-9741-6

Reviewer #3 (Public Review):

Summary:

This study explores the dynamic reprogramming of histone modification H3K4me2 during the early stages of mammalian embryogenesis. Utilizing the advanced CUT&RUN technique coupled with high-throughput sequencing, the authors investigate the erasure and re-establishment of H3K4me2 in mouse germinal vesicle (GV) oocytes, metaphase II (MII) oocytes, and early embryos.

Strengths:

The findings provide valuable insights into the temporal and spatial dynamics of H3K4me2 and its potential role in zygotic genome activation (ZGA).

Weaknesses:

The study primarily remains descriptive at this point. It would be advantageous to conduct further comprehensive functional validation and mechanistic exploration.

Key areas for improvement include enhancing the innovation and novelty of the study, providing robust functional validation, establishing a clear model for H3K4me2's role, and addressing technical and presentation issues. The text would benefit from the introduction of a novel conceptual framework or model that provides a clear explanation of the functional consequences and molecular mechanisms underlying H3K4me2 reprogramming in the transition from parental to early embryonic development.

While the findings are significant, the current manuscript falls short in several critical areas. Addressing major and minor issues will significantly strengthen the study's contribution to the field of epigenetic reprogramming and embryonic development.

eLife Assessment

This study characterizes several novel activities of SARS-CoV-2 helicase nsp13, providing valuable insights into potentially new functions of this essential RNA-processing enzyme in the virus life cycle. However, the experimental evidence to support the authors' claims is incomplete. In addition, the placement of the polyhistidine affinity tag on nsp13 may cause artifacts, raising concerns about the interpretation of the results.

Reviewer #1 (Public review):

In the manuscript by Li et al., the authors perform a comprehensive study on the template and cofactor determinants of the SARS-CoV-2 nsp13 protein. They find that, alongside the classical processive unwinding ability of helicases driven by ATP consumption, other chaperone-like and ATP-independent functions exist for this enzyme. By testing DNA and RNA oligos in several conformations, the authors show that these functions are highly dependent on template identity, but also on the ratio of ATP to divalent cations. Ultimately, it is suggested that these distinct mechanisms of action are employed by nsp13 to orchestrate viral replication.

Overall, this study provides some novel insights into the functionality of a central and conserved enzyme of a relevant human pathogenic virus. While the approach is important and adds to the field, particularly by characterizing the chaperoning activities and adding G-quadruplexes as templates, previous studies have already identified several determinants of nsp13 template binding and processing in vitro (Sommers et al., 2023, JBC; Park et al., 2025, JBC). In addition, some issues regarding experimental design need to be addressed to increase the cogency and biological relevance of the study.

(1) Generally, low concentrations of monovalent cations (20 mM), as used throughout this study, may influence helicase activity and artificially enhance protein binding/oligomerization, which could favor the observed chaperoning activity (Venus et al., 2022, Methods). In contrast, some helicases, such as HCV NS3, are inhibited by higher K+ concentrations (Gwack et al., 2004, FEBS). Thus, the influence of higher concentrations of monovalent cations should be tested in relevant assays, as intracellular K+ levels are usually >100 mM. Additionally, this could significantly affect template stability. For instance, in some G4 assays, the addition of the trap already leads to observable duplex formation (Figure 5), which may be due to low K+ conditions.

(2) As in most publications that focus strictly on helicase (or other enzymatic) functions, the activity of the isolated protein is examined. However, particularly in the case of nsp13, core functions rely on other factors, such as nsp7/8 and other components of the replication-transcription complex (RTC). The overall structure and oligomerization state of nsp13 are altered within the complex (Chen et al., 2022, NSMB). The inclusion of such factors in key experiments would greatly improve the biological relevance of the findings.

(3) In Figure 4, the authors claim that Mg2+ concentration inhibits RNA unwinding. While this is likely considering previous findings, it must be validated that duplex stabilization is not the primary cause for the observed lower dissociation rates. As the template is only 12 bp long with extensive overhangs, higher ion concentrations may significantly stabilize base pairing by reducing fraying effects. Similarly, in Figure 6, template-dependent effects of Mg2+/ATP should be ruled out.

(4) It is not entirely clear to me by which principle the templates were chosen. In my opinion, it would improve the overall comparability of the experimental results if, for instance, the blunt-ended duplex had the same sequence as the oligos with overhangs, since factors such as length, G/C content, Tm, etc., may play a significant role in binding and unwinding. Similarly, the oligos for binding and unwinding should be kept somewhat comparable, e.g., the G4 for the binding assay has 3 stacks, whereas RG1 has only 2. This discrepancy could make a significant difference. Thus, key experiments should be repeated using comparable sequence pairs.<br /> Moreover, in the initial characterization of the binding abilities (Figure 1), the authors should include blunt-ended controls (duplex/hairpin) and, importantly, a pseudoknot (PK), as these structures are crucial for multiple steps in the viral life cycle (frameshifting, replication). Specifically, the PK in the 3'UTR (Sola et al., 2011, RNA Biology) may be an interesting target structure for unwinding assays, as it recruits the RTC, and, to my knowledge, no studies are available regarding nsp13 function at a PK. This would be particularly interesting in combination with nsp7/8 (Ohyama et al., 2024, JACS Au).

Reviewer #2 (Public review):

Summary:

The authors are trying to broaden the understanding of SARS-CoV2 Nsp13 activity to show that a single viral protein can accomplish multiple functions. Additionally, they try to show that helicase function is not limited to ATP-driven, unidirectional unwinding.

Strengths:

The consistent application of statistics to triplicate experiments is a strength of the manuscript. The ToPif1 control in Figure S12 is a good control.

Weaknesses:

(1) All the experiments except the one in Figure S2 use N-terminally His-tagged Nsp13. Because the N-terminal tag is known to have large effects on Nsp13 activity, this calls into question virtually all of the results in this manuscript.

(2) The ATP-independent, bidirectional duplex unwinding shown for short duplex substrates is reminiscent of the trapping of thermal fraying intermediates that have been reported for other helicases. Because they are only observed on short duplexes, do not require ATP, and are bidirectional, this does not suggest strand displacement as suggested in the manuscript. Instead, it suggests trapping of partially melted intermediates.

(3) Results that may be artifacts of unusual in vitro conditions are interpreted as if similar results will occur in the cell, where ATP is likely always present. Along those same lines, SARS-CoV-2 replicates in compartments of the endoplasmic reticulum, which would limit the ability of Nsp13 to access DNA substrates.

(4) There is no evidence to support the conclusion that "Duplex DNA supports bidirectional remodeling via both ATP-dependent and ATP-independent mechanisms." 3'-5' duplex melting is limited to short duplexes and is ATP-independent, suggesting it may be due to trapping of thermal fraying intermediates by the ssDNA binding Nsp13. The ATP-dependent and ATP-independent melting on the substrates with the 3'-overhang are the same, suggesting that ATP-dependent melting does not occur on this substrate, which would indicate that bidirectional ATP-dependent translocation does not occur.

(5) The description of ATP-independent unwinding as having "limited processivity," is likely not accurate. These experiments were multiturnover reactions with very high Nsp13 concentrations and no protein trap to ensure single turnover conditions. Because the reactions were multi-turnover, no information about the processivity of Nsp13 can be obtained. On the contrary, it seems likely that the product formed over the 30-minute reaction with a vast excess of Nsp13 is due to binding and dissociation of multiple Nsp13 molecules instead of processive translocation by a single enzyme.

(6) G4s are much more stable at cellular K+ concentrations than they are at 20 mM K+. As such, Nsp13's ability to unfold a G4 in the absence of ATP may be diminished or eliminated at a physiological K+ concentration.

Although the authors show that His-tagged Nsp13 can melt DNA and RNA duplexes and G-quadruplexes in an ATP-dependent and independent manner, in addition to annealing single-stranded nucleic acids into duplexes, the use of His-tagged Nsp13, which is known to cause artifacts, makes their results difficult to draw conclusions from. As such, in the opinion of this reviewer, this manuscript is likely to have little impact on the field.

Author response:

Public Reviews:

Reviewer #1 (Public review):

In the manuscript by Li et al., the authors perform a comprehensive study on the template and cofactor determinants of the SARS-CoV-2 nsp13 protein. They find that, alongside the classical processive unwinding ability of helicases driven by ATP consumption, other chaperone-like and ATP-independent functions exist for this enzyme. By testing DNA and RNA oligos in several conformations, the authors show that these functions are highly dependent on template identity, but also on the ratio of ATP to divalent cations. Ultimately, it is suggested that these distinct mechanisms of action are employed by nsp13 to orchestrate viral replication.

Overall, this study provides some novel insights into the functionality of a central and conserved enzyme of a relevant human pathogenic virus. While the approach is important and adds to the field, particularly by characterizing the chaperoning activities and adding G-quadruplexes as templates, previous studies have already identified several determinants of nsp13 template binding and processing in vitro (Sommers et al., 2023, JBC; Park et al., 2025, JBC). In addition, some issues regarding experimental design need to be addressed to increase the cogency and biological relevance of the study.

We thank the reviewer for recognizing the novelty of our work, particularly the ATP-independent chaperone-like activities and G-quadruplex remodeling. We also appreciate the opportunity to clarify the conceptual distinction between our study and the prior work by Sommers et al. (2023) and Park et al. (2025). We fully agree that those studies systematically defined the canonical ATP-driven motor mechanism of Nsp13. Our results on 5′→3′ polarity, DNA preference, and tail/ATP/Mg²⁺ dependence align with these benchmarks, confirming the reliability of our platform.

However, the core novelty of our work lies in revealing that Nsp13 functions as a multifaceted nucleic acid remodeler, integrating motor and non-motor activities within a single protein-a functional regime absent from the JBC papers. Specifically, we uncover three novel layers: 1. Mg²⁺-activated, ATP-independent remodeling of short duplexes and G-quadruplexes. 2. Bidirectional remodeling on duplexes in the Mg²⁺-primed state. 3. Intrinsic chaperone functions including strand annealing and stem-loop restructuring.

Thus, our work fundamentally expands the biochemical model of Nsp13 from a simple ATP-driven motor to a multifunctional, mode-switchable remodeler. We will highlight these distinctions in the revised Discussion. Below, we respond point-by-point to the specific experimental design issues.

(1) Generally, low concentrations of monovalent cations (20 mM), as used throughout this study, may influence helicase activity and artificially enhance protein binding/oligomerization, which could favor the observed chaperoning activity (Venus et al., 2022, Methods). In contrast, some helicases, such as HCV NS3, are inhibited by higher K+ concentrations (Gwack et al., 2004, FEBS). Thus, the influence of higher concentrations of monovalent cations should be tested in relevant assays, as intracellular K+ levels are usually >100 mM. Additionally, this could significantly affect template stability. For instance, in some G4 assays, the addition of the trap already leads to observable duplex formation (Figure 5), which may be due to low K+ conditions.

We thank the reviewer for this critical comment regarding the ionic environment. We agree that monovalent cation concentrations are pivotal for both helicase activity and the structural stability of templates like G4s.

First, we wish to clarify that the final NaCl concentration in our reaction is not 20 mM, as this refers only to the unwinding buffer. Our protein dilution buffer contains 200 mM NaCl, and each 10 μL reaction includes 2 μL of protein, contributing ~40 mM NaCl. With 20 mM from the reaction buffer, the final concentration reaches~60 mM. We will clarify this in the Methods.

Second, our choice of ionic strength is guided by established literature. A survey of 27 published nsp13 studies (Author response table 1) shows that the majority use 20–50 mM monovalent cations, with 20 mM being most common. Mickolajczyk et al. (2021) showed that nsp13 activity is highest at low salt and declines at higher concentrations. Thus, low salt conditions are routinely used to capture nsp13’s intrinsic catalytic activity. The intracellular environment is far more complex, with crowding and interacting proteins that likely modulate helicase behavior. The low-salt conditions are therefore a deliberate simplification to isolate and define enzyme function.

Planned experiments: We fully agree that higher salt concentrations should be tested. In the revision, we will perform key assays such as ATP-independent duplex unwinding and G4 unfolding at ≥100 mM NaCl or KCl to verify that the observed activities persist under more physiological ionic conditions

(2) As in most publications that focus strictly on helicase (or other enzymatic) functions, the activity of the isolated protein is examined. However, particularly in the case of nsp13, core functions rely on other factors, such as nsp7/8 and other components of the replication-transcription complex (RTC). The overall structure and oligomerization state of nsp13 are altered within the complex (Chen et al., 2022, NSMB). The inclusion of such factors in key experiments would greatly improve the biological relevance of the findings.

We agree that examining Nsp13 within the context of the RTC is essential for establishing the biological relevance of our findings. The structural reorganization of Nsp13 upon binding to Nsp12 and Nsp7/8 (Chen et al., 2022) suggests that its enzymatic "mode" may be regulated by its protein partners.

Planned experiments: To address this, we will include the following biochemical characterizations:

(1) Nsp13/12 and Nsp13/7/8 sub-complexes will be examined to dissect the individual contributions of the polymerase and the primase-like factors to Nsp13’s multifaceted activities.

(2) The core RTC (Nsp13/12/7/8) will be used to evaluate how the full assembly modulates the functions of Nsp13 particularly on complex templates like G4 and pseudoknots.

(3) In Figure 4, the authors claim that Mg2+ concentration inhibits RNA unwinding. While this is likely considering previous findings, it must be validated that duplex stabilization is not the primary cause for the observed lower dissociation rates. As the template is only 12 bp long with extensive overhangs, higher ion concentrations may significantly stabilize base pairing by reducing fraying effects. Similarly, in Figure 6, template-dependent effects of Mg2+/ATP should be ruled out.

We thank the reviewer for this insightful suggestion. We agree that it is critical to distinguish whether the observed inhibition of RNA unwinding at higher Mg²⁺ concentrations is due to the physical stabilization of the RNA duplex.

Planned experiments: To address this, we will perform the following characterizations:

(1) We will measure the Tm of the RNA duplex used in Figure 4 across a range of Mg²⁺ concentrations (0, 0.5, and 1.0 mM). This will allow us to quantify the extent to which divalent cations stabilize the duplex RNA. These data will provide a more rigorous interpretation of the Mg²⁺-dependent unwinding in Figure 4.

(2) Similarly, we will perform thermal melting analyses for the various DNA and RNA templates used in Figure 6 under different Mg²⁺/ATP conditions to rule out the template-dependent effects of Mg²⁺/ATP.

(4) It is not entirely clear to me by which principle the templates were chosen. In my opinion, it would improve the overall comparability of the experimental results if, for instance, the blunt-ended duplex had the same sequence as the oligos with overhangs, since factors such as length, G/C content, Tm, etc., may play a significant role in binding and unwinding. Similarly, the oligos for binding and unwinding should be kept somewhat comparable, e.g., the G4 for the binding assay has 3 stacks, whereas RG1 has only 2. This discrepancy could make a significant difference. Thus, key experiments should be repeated using comparable sequence pairs.

We fully agree with the reviewer that maintaining sequence consistency across different assays is essential for a rigorous comparison of nsp13 activities. We apologize for the ambiguity in the initial presentation of our sequences in Table S1.

Planned revisions and experiments:

(1) We wish to clarify that several key substrates were sequence-matched. For unwinding assays, the 12-bp 3′-overhang DNA and blunt-ended DNA share the identical duplex sequence, and the 16-bp 5′-overhang and 3′-overhang DNA substrates are also sequence-matched. For annealing assays, the duplex regions for all DNA substrates (3′, 5′, blunt, and fork) are identical, and the same internal consistency was maintained for all RNA annealing substrates. To make this clear, we will reorganize Table S1 to explicitly group these sequence-paired substrates.

(2) The reviewer also notes discrepancies between binding and unwinding substrates (e.g., the difference in G4 stacks). To ensure direct comparability, we will perform additional experiments: complete binding assays for RG-1 (the 2-stack G4 used in unwinding) to match the functional data, and systematically measure binding affinities for all key unwinding substrates, including 3′-overhang, 5′-overhang, blunt-ended DNA, and the RNA fork.

(5) Moreover, in the initial characterization of the binding abilities (Figure 1), the authors should include blunt-ended controls (duplex/hairpin) and, importantly, a pseudoknot (PK), as these structures are crucial for multiple steps in the viral life cycle (frameshifting, replication). Specifically, the PK in the 3'UTR (Sola et al., 2011, RNA Biology) may be an interesting target structure for unwinding assays, as it recruits the RTC, and, to my knowledge, no studies are available regarding nsp13 function at a PK. This would be particularly interesting in combination with nsp7/8 (Ohyama et al., 2024, JACS Au).

We thank the reviewer for this insightful and inspiring suggestion. Incorporating pseudoknot (PK) structures into our analysis—particularly the well-characterized PK in the 3'UTR (Sola et al., 2011)—represents a significant opportunity to bridge our biochemical findings with the viral life cycle. To address this, we have designed a 3'UTR PK substrate based on recently reported scaffolds (Ohyama et al., 2024).

Planned experiments:

(1) We will expand our initial binding assays (Figure 1) to include blunt-ended duplexes, hairpins, and the 3'UTR PK. This will establish a baseline for how Nsp13 recognizes these structurally distinct and physiologically critical templates.

(2) We will perform unwinding assays to determine whether Nsp13, in its isolated state, possesses the mechanical capability to resolve the complex tertiary interactions within a pseudoknot.

(3) Following the reviewer's insight, we will examine whether the addition of nsp7/8 is required to facilitate the unfolding of the 3'UTR PK.

Together, these experiments will allow us to assess whether Nsp13 is capable of managing one of the most challenging structural obstacles in the SARS-CoV-2 genome.

Reviewer #2 (Public review):

Summary:

The authors are trying to broaden the understanding of SARS-CoV2 Nsp13 activity to show that a single viral protein can accomplish multiple functions. Additionally, they try to show that helicase function is not limited to ATP-driven, unidirectional unwinding.

Strengths: The consistent application of statistics to triplicate experiments is a strength of the manuscript. The ToPif1 control in Figure S12 is a good control.

We thank the reviewer for the insightful assessment and for highlighting the rigor of our experimental design, particularly our reliance on triplicate data with robust statistical validation and the inclusion of the ToPif1 control.

We are especially grateful for the detailed comments provided by the reviewer. We fully recognize that addressing these specific points is essential for strengthening the cogency of our conclusions and improving the overall rigor of the manuscript. These suggestions have provided us with a clear roadmap for further refining our experimental evidence and clarifying our mechanistic interpretations. Below, we respond point-by-point to the specific issues.

Weaknesses:

(1) All the experiments except the one in Figure S2 use N-terminally His-tagged Nsp13. Because the N-terminal tag is known to have large effects on Nsp13 activity, this calls into question virtually all of the results in this manuscript.

We thank the reviewer for raising this important concern regarding the potential influence of the N-terminal His tag on nsp13 activity. We have carefully considered this issue and provide the following lines of evidence to address it.

(1) We have generated a tag-free nsp13 variant and our preliminary characterization (Author response image 1) shows that it retains all key activities: ATP hydrolysis (comparable to His-tagged nsp13), both ATP-independent (Mg²⁺-activated) and ATP-dependent unwinding, as well as chaperone activity to remodel stem-loops. These results demonstrate that while the His tag may modulate enzymatic efficiency, it does not create or abolish any specific biochemical function.

(2) We conducted a systematic survey of 27 published studies on SARS-CoV/SARS-CoV-2 nsp13 (Author response table 1). The results show that 17 out of 27 studies (63%) used affinity-tagged nsp13 without tag removal, including His, MBP, GST, and Strep tags.

(3) The only study that systematically compared different affinity tags (Adedeji et al., 2012) reported that GST-tagged nsp13 exhibited ~520-fold higher ATPase activity than His-tagged nsp13, demonstrating that the choice of affinity tag can affect enzymatic efficiency. However, both tagged versions retained all core enzymatic activities, including ATP hydrolysis and duplex unwinding. Importantly, no study has compared the full functional spectrum between His-tagged and tag-free nsp13. Our preliminary data suggest that the His tag may affect efficiency but does not alter the presence or absence of any specific activity.

Planned experiments:

We fully agree with the reviewer that a more systematic comparison would strengthen the conclusions. In the revision, we will include additional characterization of tag-free nsp13: (i) quantitative nucleic acid binding affinity, (ii) G4 unfolding efficiency, (iii) strand annealing activity. These experiments are currently underway.

In summary, while we acknowledge that the His tag may influence enzymatic efficiency, our key conclusions are supported by experiments with tag-free nsp13. We will add a discussion of these points and include additional tag-free nsp13 data in the revised manuscript.

(2) The ATP-independent, bidirectional duplex unwinding shown for short duplex substrates is reminiscent of the trapping of thermal fraying intermediates that have been reported for other helicases. Because they are only observed on short duplexes, do not require ATP, and are bidirectional, this does not suggest strand displacement as suggested in the manuscript. Instead, it suggests trapping of partially melted intermediates.

We thank the reviewer for this insightful perspective. While the passive trapping of thermal fraying intermediates is a well-established model for non-catalytic protein-nucleic acid interactions, several lines of evidence suggest that nsp13 employs a more active, allosteric mechanism for ATP-independent remodeling.

(1) If nsp13 were merely a passive trap, increasing duplex stability should decrease unwinding. However, as shown in Figure S3, raising Mg²⁺ from 0 to 5 mM increases the DNA duplex Tm by ~10°C, yet nsp13’s remodeling activity is markedly enhanced under the same conditions (Figure 2). This positive correlation between cation-induced substrate stabilization and protein activation supports an active, protein-centered mechanism that overcomes the increased energetic barrier.

(2) The observed bidirectionality in ATP-independent remodeling does not simply imply a lack of polarity; rather, it can reflect nsp13’s intrinsic chaperone function. In the absence of ATP, nsp13 binds the ss/ds junction (Figure 2F) and, in a Mg²⁺-dependent manner, may use its binding energy to actively intercalate into the duplex. This mechanism is inherently symmetric for 3′ and 5′ overhangs, explaining bidirectional remodeling, while the absence of activity on blunt-ended substrates confirms the requirement for a pre-existing junction.

(3) The lack of activity on 24-bp substrates does not negate this remodeling mode but defines its energetic boundary. The binding energy released upon nsp13-nucleic acid interaction is sufficient to overcome the lower unwinding barrier of 12-16 bp duplexes, but insufficient to counteract the high stability and rapid re-annealing of a 24-bp duplex without the continuous mechanical power of ATP hydrolysis.

Planned Revision:

We thank the reviewer for prompting us to refine our mechanistic model. In the revision, we will add a dedicated discussion explicitly comparing the model of allosterically activated, binding-driven strand intrusion with the passive trapping model, incorporating the Tm data to strengthen our conclusions.

(3) Results that may be artifacts of unusual in vitro conditions are interpreted as if similar results will occur in the cell, where ATP is likely always present. Along those same lines, SARS-CoV-2 replicates in compartments of the endoplasmic reticulum, which would limit the ability of Nsp13 to access DNA substrates.

We thank the reviewer for raising this important concern regarding the physiological relevance. We fully agree that in vitro conditions do not entirely recapitulate the complex intracellular environment, and we have been careful not to over-interpret our findings. Below we address the two specific issues raised:

(1) Regarding the ATP-independent activity, we acknowledge that ATP is abundant in healthy, actively replicating cells. However, during rapid viral replication, local ATP concentrations can fluctuate due to the high energy demand of the RTC as the template contains extensive secondary structures, which may lead to transient ATP depletion. Under such energy-limited conditions, Yu et al. (2025) demonstrated that ADP-bound nsp13 exhibits chaperone activity that destabilizes nucleic acid structures without ATP hydrolysis, and Dumm et al. (2025) reported that SARS-CoV-2 nsp13 resolves RNA stem-loops in an ATP-independent manner.

Even when ATP is abundant, the ATP-independent mode may enable rapid, local structural adjustments that bypass the kinetic delay of ATP binding and hydrolysis. As shown in Figure 1D, nsp13 exhibits high binding affinity for structured nucleic acids. In this scenario, nsp13 functions not as a processive motor but through a binding-driven mechanism, using the free energy of protein-nucleic acid interaction to transiently destabilize short duplexes or resolve local secondary structures such as G4s and stem-loops in an energy-efficient manner.

(2) Regarding DNA substrates, we fully agree that RNA is the physiological substrate for nsp13. However, DNA is a validated and widely accepted surrogate for mechanistic studies because DNA is more stable and easier to manipulate than RNA to yield the mechanistic insights. A systematic survey of 27 published nsp13 studies (Author response table 1) shows that 20 out of 27 (74%) used DNA substrates for at least some of their experiments. In our study, we used DNA primarily as a mechanistic probe and a stable control, and we validated all key conclusions on physiological RNA substrates, as shown in Figures 4, 5, 6, S7, S8, S10, S11 and S12.

Planned revisions: To address the reviewer’s concerns more directly, we will revise the manuscript to include a discussion paragraph explicitly stating that the ATP-independent activity was observed under optimized in vitro conditions and may represent a latent remodeling capability that could be relevant under energy-limited conditions such as local ATP depletion during rapid replication. We will also clarify that DNA substrates were used as mechanistic probes and controls, and that all key findings were validated on physiological RNA substrates. We thank the reviewer for prompting us to strengthen the discussion of these important points.

(4) There is no evidence to support the conclusion that "Duplex DNA supports bidirectional remodeling via both ATP-dependent and ATP-independent mechanisms." 3'-5' duplex melting is limited to short duplexes and is ATP-independent, suggesting it may be due to trapping of thermal fraying intermediates by the ssDNA binding Nsp13. The ATP-dependent and ATP-independent melting on the substrates with the 3'-overhang are the same, suggesting that ATP-dependent melting does not occur on this substrate, which would indicate that bidirectional ATP-dependent translocation does not occur.

We are grateful to the reviewer for this critical evaluation of our mechanistic claims. We agree that our initial statement regarding bidirectional ATP-dependent remodeling was imprecise and not fully supported by the data. As the reviewer correctly notes, the similar unwinding efficiency on 3′-overhang substrates regardless of ATP presence indicates that ATP hydrolysis does not drive 3′→5′ translocation, which is consistent with nsp13’s known 5′→3′ motor polarity. The observed 3′→5′ activity is therefore more accurately described as an ATP-independent remodeling event, not ATP-dependent unwinding.

We will revise the Discussion and relevant Results sections to clarify the nature of this bidirectional activity. Specifically, the sentence:

"Duplex DNA supports bidirectional remodeling via both ATP-dependent and ATP-independent mechanisms..."will be corrected to: "Duplex DNA supports bidirectional remodeling via ATP-independent mechanisms."

We will also explicitly state that while nsp13 requires ATP for long-range, processive 5'→3' helicase activity, its remodeling/chaperone function is inherently bidirectional and powered by the free energy of binding to the ss/ds junction, rather than by ATP-driven mechanical work.

(5)-The description of ATP-independent unwinding as having "limited processivity," is likely not accurate. These experiments were multiturnover reactions with very high Nsp13 concentrations and no protein trap to ensure single turnover conditions. Because the reactions were multi-turnover, no information about the processivity of Nsp13 can be obtained. On the contrary, it seems likely that the product formed over the 30-minute reaction with a vast excess of Nsp13 is due to binding and dissociation of multiple Nsp13 molecules instead of processive translocation by a single enzyme.

We thank the reviewer for this important correction. We fully agree that our use of the term "processivity" was technically imprecise. Processivity strictly defines the distance a single enzyme translocates during one binding event, which our multi-turnover assays (with high nsp13 concentrations and no protein trap) were not designed to measure. Our results specifically demonstrate that the ATP-independent remodeling mode is highly sensitive to duplex length, with efficiency declining sharply as the duplex lengthens. To reflect the experimental data more faithfully, we have replaced "processivity" with more accurate descriptors throughout the manuscript.

Planned revisions:

(1) Original: "The ATP-independent unwinding mode, however, has limited processivity." Revised: "The ATP-independent unwinding mode, however, exhibits a steep decline in efficiency as the duplex length increases."

(2) Original: "...an ATP-independent, cation-activated mode with limited processivity." Revised: "...an ATP-independent, cation-activated mode specialized for localized structural remodeling"

(3) Original: "...primes Nsp13 for basal strand remodeling but supports only limited processivity." Revised: "...primes Nsp13 for basal strand remodeling but is insufficient for the sustained unwinding of extended duplexes."

(4) Original: "...primes Nsp13 for low-processivity strand displacement." Revised: "...primes Nsp13 for short-range strand displacement rather than long-range processive unwinding."

We believe these changes clarify that the ATP-independent mode acts as a molecular chaperone for local obstacles (like G4 or short stems) rather than a motor for long-range translocation. We thank the reviewer for helping us improve the precision of our description.

(6) G4s are much more stable at cellular K+ concentrations than they are at 20 mM K+. As such, Nsp13's ability to unfold a G4 in the absence of ATP may be diminished or eliminated at a physiological K+ concentration.

We thank the reviewer for this critical point regarding physiological ion concentrations. We agree that K⁺ significantly stabilizes G4 structures, which may raise the energy barrier for ATP-independent remodeling.

Planned experiments:

To address this, we will perform salt titration assays (up to 150 mM KCl) to evaluate the robustness of nsp13’s G4 unfolding activity under more physiological ionic conditions. We will also measure the melting temperature of our G4 substrates across this K⁺ range to correlate structural stability with enzymatic efficiency.

Author response image 1.

Preliminary characterization of tag-free Nsp13 enzymatic activities. (A) Comparison of ATPase activity between His-tagged and tag-free Nsp13 in the presence of ssRNA or RNA G4. (B) Raw fluorescence data from stopped-flow FRET analysis of ATP-dependent unwinding (16-bp fork DNA, 2 mM Mg²⁺, 2 mM ATP). F/F₀ represents FAM fluorescence normalized to initial DNA intensity. (C) ATP-independent DNA duplex remodeling (data reproduced from Figure S2). (D) Chaperone activity of tag-free Nsp13 on DNA and RNA stem-loops.

Author response table 1.

Summary of affinity tags, monovalent salt concentrations, and substrate types used in 27 published SARS-CoV/SARS-CoV-2 nsp13 studies

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(8) Yazdi AK, Pakarian P, Perveen S, Hajian T, Santhakumar V, Bolotokova A, Li F, Vedadi M. Kinetic Characterization of SARS-CoV-2 nsp13 ATPase Activity and Discovery of Small-Molecule Inhibitors. ACS Infect Dis. 2022 Aug 12;8(8):1533-1542.

(9) Corona A, Wycisk K, Talarico C, Manelfi C, Milia J, Cannalire R, Esposito F, Gribbon P, Zaliani A, Iaconis D, Beccari AR, Summa V, Nowotny M, Tramontano E. Natural Compounds Inhibit SARS-CoV-2 nsp13 Unwinding and ATPase Enzyme Activities. ACS Pharmacol Transl Sci. 2022 Apr 1;5(4):226-239.

(10) Lu L, Peng Y, Yao H, Wang Y, Li J, Yang Y, Lin Z. Punicalagin as an allosteric NSP13 helicase inhibitor potently suppresses SARS-CoV-2 replication in vitro. Antiviral Res. 2022 Oct;206:105389.

(11) Yue K, Yao B, Shi Y, Yang Y, Qian Z, Ci Y, Shi L. The stalk domain of SARS-CoV-2 NSP13 is essential for its helicase activity. Biochem Biophys Res Commun. 2022 Apr 23;601:129-136.

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eLife Assessment

This useful study presents an improved protocol for long-term in vitro culture of Schistosoma mansoni that enables progression toward sexually dimorphic stages, representing a meaningful advance for studying parasite development and reducing reliance on animal models. The findings show that host-specific culture conditions support essential developmental and metabolic functions required for parasite maturation, although development remains delayed compared to in vivo conditions. The evidence is solid overall, but limited pairing efficiency and the absence of egg production indicate that the system does not yet fully recapitulate complete reproductive development.

Reviewer #1 (Public review):

Pichon, Rémi et al. describe an in vitro method for transforming Schistosoma cercariae into mature adult worms. The authors show that human serum (HS) supports parasite growth and differentiation more effectively than fetal bovine serum (FBS). They also observed differences in parasite growth and activity, with worms cultured in HS efficiently digesting human red blood cells (hRBC). Cultured worms were able to pair with ex vivo adult worms and produce eggs, indicating functional maturation suitable for downstream applications such as drug screening. While the experimental approach is comprehensive and supports the advantages of HS culture conditions, the pairing efficiency was low (≈7%) and required long culture periods (70-80 days), highlighting limitations that may affect reproducibility.

A major strength of the study, in particular, is that the authors clearly differentiate the effects of FBS versus HS on developmental progression. The conversion rate observed in HS cultures is significant and consistent with previously published data.

While the study has several strengths, some aspects of the work are not fully explored. In particular, the role of hRBC supplementation requires further clarification. Although HS-cultured worms were shown to digest hRBC more readily, the implications of this observation remain unclear. Specifically, it would be useful to understand whether hRBC supplementation influences (1) long-term culture stability, (2) molecular pathways associated with development and differentiation, or (3) the pairing capacity of the worms. While addressing these questions may not be the main objective of the study, further discussion of these points would strengthen the manuscript.

The manuscript is clearly written and represents a valuable contribution to the field. Overall, the experimental approach is sound, and the results support a useful methodological framework for the in vitro culture of Schistosoma worms and the attainment of sexual maturity, particularly for adult male worms.

Reviewer #2 (Public review):

Summary:

The authors perform confirmation studies of Paul Basch's seminal schistosome work from 1981, demonstrating the development of transformed schistosomules into sexually dimorphic adult parasites, albeit without successful egg production. In addition to the findings from Basch's earlier work, the authors add some new molecular data in the form of an analysis of proliferative cells in in-vitro-derived animals.

Strengths:

The authors successfully confirm experimental results from earlier schistosome researchers, providing a potential new tool for studying schistosome biology without the need for vertebrate hosts.

Weaknesses:

The display of data from the authors is sometimes difficult to follow/understand where it comes from. For example:

(1) Line 136: The authors claim that parasites in HS and FBS conditions have substantially different mortality rates (11.3 +/- 2.7 vs 5 +/- 2.3) but a quite high p-value (0.8). Analyzing the raw data myself, I obtained a mean of 8.2 +/- 1.7% vs 4.8% +/- 4.3% with a p-value of 0.15. Either the data are not clearly presented, and I did not follow them, or the data presented in the text do not match the raw data in the supplemental files.

(2) Line 187/Figure 4: Though it is not clearly stated, it appears that the authors treat their EdU counts as an ordinal data set of 61 steps (from 0 to >60) rather than a continuous measure of EdU+ cells per animal. In this author's opinion, the graph strongly suggests a continuous data set, and the fact that this reviewer had to dig through poorly-labeled raw data to discover the nature of the data is problematic. The authors should either switch to a continuous data set or make it explicit that the data shown are ordinal. If counting EdU+ cells is too arduous, the authors could consider comparing the amount of EdU+ area to the amount of DAPI+ area in maximum intensity projections of their confocal images, as this would roughly approximate the amount of proliferative cells in the animals.

There are some minor issues as well:

(1) Line 122: It is perhaps incorrect to refer to humans as "the" definitive host of schistosomes, as S. japonicum is primarily considered a zoonotic infection with water buffalo/cows being the primary definitive host.

(2) Line 185/298: The authors refer to EdU pulse-chase experiments, but the experiments described here are EdU pulse experiments.

Reviewer #3 (Public review):

Summary:

This study is significant as it established a protocol for the long-term culture of Schistosoma mansoni newly transformed cercariae, which developed in vitro into sexually dimorphic forms. The impact of two different sera, Fetal Bovine Serum (FBS) and Human Serum (HS), added to the culture medium supplemented with human red blood cells was evaluated. The authors demonstrated that HS-cultured parasites were able to digest red blood cells, a critical step for long-term parasite development. Furthermore, while most FBS-cultured parasites did not progress beyond an early liver stage, sexual dimorphism was clearly evident in the HS-cultured worms, albeit delayed compared to in vivo development.

Strengths:

This study could contribute to further in vitro studies for a better understanding of the unique sexual biology of Schistosoma mansoni and for screening novel schistosomicidal compounds. By increasing parasite development in in vitro studies, this protocol could have a positive impact on the principles of the 3Rs (Replacement, Reduction and Refinement) for animal research.

Weaknesses:

As the authors mentioned, "pairing between male and female parasites was rare. Pairing was observed in approximately ~7% of the experiments, usually after day ~ 80 in culture. Egg production was also not achieved with this protocol.

Author response:

eLife Assessment

This useful study presents an improved protocol for long-term in vitro culture of Schistosoma mansoni that enables progression toward sexually dimorphic stages, representing a meaningful advance for studying parasite development and reducing reliance on animal models. The findings show that host-specific culture conditions support essential developmental and metabolic functions required for parasite maturation, although development remains delayed compared to in vivo conditions. The evidence is solid overall, but limited pairing efficiency and the absence of egg production indicate that the system does not yet fully recapitulate complete reproductive development.

On behalf of the co-authors, we thank the three reviewers and the editors for their complimentary remarks as well as the major and minor comments/ concerns. Addressing these concerns have led to revisions that improved the manuscript. In particular, further analyses have generated an updated Figures 3 and 4, and Supplementary Tables S1, and S4-S6.

Public Reviews:

Reviewer #1 (Public review):

Pichon, Rémi et al. describe an in vitro method for transforming Schistosoma cercariae into mature adult worms. The authors show that human serum (HS) supports parasite growth and differentiation more effectively than fetal bovine serum (FBS). They also observed differences in parasite growth and activity, with worms cultured in HS efficiently digesting human red blood cells (hRBC). Cultured worms were able to pair with ex vivo adult worms and produce eggs, indicating functional maturation suitable for downstream applications such as drug screening. While the experimental approach is comprehensive and supports the advantage of HS culture conditions, the pairing efficiency was low (≈7%) and required long culture periods (70-80 days), highlighting limitations that may affect reproducibility.

We acknowledge the reviewer for the positive highlights. Regarding the low in vitro pairing efficiency, we have now edited the manuscript to clarify a misleading statement related to 7%. We decided to remove the value of 7% — which corresponds to the percentage of experiments in which couples were observed, as it does not accurately represent the actual number of observed worm pairs and it is probably misleading. We have updated the text as follows:

Results, lines 230 ff.:

“While the establishment of sexual dimorphism was robust and reproducible across more than 15 independent experiments, pairing between male and female parasites was rare. Pairing was observed only in experiments lasting more than 80 days in which we were only able to observe a few couples. In addition, these pairings were temporary (Figures 6A, B; Supplementary Video S4).”

We also agree with the reviewer that the extended culture periods required to obtain fully sexually dimorphic parasites remain a limitation. As elaborated in Discussion (see below), key factors, probably derived from the host, are missing in the in vitro system explaining both the slow in vitro development and low rate of spontaneous pairing between in vitro developed, sexually dimorphic male and female worms. This was discussed as follows (lines 340-343): “That said, while our system was highly efficient in producing sexually dimorphic worms, spontaneous pairing between male and female parasites was extremely rare, mainly in aged in vitro cultures (from 80 to 100 days in culture) indicating that other factors, e.g., cholesterol, may be missing[35].”

A major strength of the study, in particular, is that the authors clearly differentiate the effects of FBS versus HS on developmental progression. The conversion rate observed in HS cultures is significant and consistent with previously published data.

While the study has several strengths, some aspects of the work are not fully explored. In particular, the role of hRBC supplementation requires further clarification. Although HS-cultured worms were shown to digest hRBC more readily, the implications of this observation remain unclear. Specifically, it would be useful to understand whether hRBC supplementation influences (1) long-term culture stability, (2) molecular pathways associated with development and differentiation, or (3) the pairing capacity of the worms. While addressing these questions may not be the main objective of the study, further discussion of these points would strengthen the manuscript.

We agree that deciphering the role of the human Red Blood Cells (hRBCs) supplementation is critical. Regarding the influence of hRBCs on the long-term culture stability in parasite development it has been well established for more than four decades that schistosomes do need red blood cells to grow in culture [Basch, P. F. Cultivation of Schistosoma mansoni in vitro. II. production of infertile eggs by worm pairs cultured from cercariae. J Parasitol 67, 186-190 (1981); Basch, P. F. Cultivation of Schistosoma mansoni in vitro. I. Establishment of cultures from cercariae and development until pairing. J. Parasitol. 67, 179-185 (1981)]. The molecular pathways underlying development, sexual differentiation and pairing and modulated by hRBCs in culture is currently being investigated by our team. We decided not to include these data and analyses in the current manuscript, as they fall outside its scope.

The manuscript is clearly written and represents a valuable contribution to the field. Overall, the experimental approach is sound, and the results support a useful methodological framework for the in vitro culture of Schistosoma worms and the attainment of sexual maturity, particularly for adult male worms.

We thank the reviewer for highlighting the manuscript’s strengths.

Reviewer #2 (Public review):

Summary:

The authors perform confirmation studies of Paul Basch's seminal schistosome work from 1981, demonstrating the development of transformed schistosomules into sexually dimorphic adult parasites, albeit without successful egg production. In addition to the findings from Basch's earlier work, the authors add some new molecular data in the form of an analysis of proliferative cells in in-vitro-derived animals.

Strengths:

The authors successfully confirm experimental results from earlier schistosome researchers, providing a potential new tool for studying schistosome biology without the need for vertebrate hosts.

We thank the reviewer for highlighting the manuscript’s strengths.

Weaknesses:

The display of data from the authors is sometimes difficult to follow/understand where it comes from. For example:

(1) Line 136: The authors claim that parasites in HS and FBS conditions have substantially different mortality rates (11.3 +/- 2.7 vs 5 +/- 2.3) but a quite high p-value (0.8). Analyzing the raw data myself, I obtained a mean of 8.2 +/- 1.7% vs 4.8% +/- 4.3% with a p-value of 0.15. Either the data are not clearly presented, and I did not follow them, or the data presented in the text do not match the raw data in the supplemental files.

We thank the reviewer for pointing this out; we have now edited Supplementary Tables S1 and S6 by turning them into a long format for the sake of clarity. Accordingly, Results, Methods sections, and indicated supplementary tables were edited as follows:

Results, lines 142 ff.:

“No morphological differences were observed between parasites cultured either in FBS or HS within the first week in culture; in both conditions most parasites were classified as early schistosomula [category 1: 76% ± 30 (average ± SD) in FBS and 73% ± 29 (average ± SD) in HS] with few lung (category 2) and early liver schistosomula (category 3) (Figure 1B, week 1; Supplementary Figure S1). The mean mortality (category 0) at week 1 was slightly higher, but not statistically significant (P= 0.42), in worms cultured in HS [9.75% ± 2.76 (average ± SD)] compared to the mortality registered in FBS-cultured parasites [5.52% ± 5.18 (average ± SD), Supplementary Table S6], consistent with previous findings[39].”

Methods, lines 463-465:

“To evaluate differences in mortality between HS- and FBS-cultured parasites, data from 5 experiments were combined and analysed using a Shapiro-Wilk normality test to test normality of the data and a non-parametric Wilcoxon rank sum exact test (Supplementary Tables S1 and S6).”

Supplementary Tables:

Supplementary Table S1. “Raw counts of parasites within each developmental stage category. Each row corresponds to a picture of parasites in culture medium containing FBS or HS. Each column corresponds to the raw parasite counts at indicated stage development (categories 0 to 5), time in culture (Time in days - D), and experimental condition.”

Supplementary Table S6. “Summary of all statistical tests employed in this study. 1. Statistical tests of parasite mortality and the raw data table used for this test. 2. Statistical tests for worm size comparisons (correspond to Figure 2). 3. Statistical tests for worm black gut comparisons (correspond to Figure 3). BG: Black gut. 4. Statistical tests for EdU positive cells comparisons (correspond to Figure 4). Replicate code: E, M and L correspond to day 2, 8 and 15 respectively; R and W correspond to the presence (R) or absence (W) of RBCs added 13 days after transformation.”

For clarity, in Author response image 1 we provide the R script used to perform the statistical tests on the data shown in Supplementary Table S6 (column Raw count of parasite developmental category per image and experiment)

Author response image 1.

(2) Line 187/Figure 4: Though it is not clearly stated, it appears that the authors treat their EdU counts as an ordinal data set of 61 steps (from 0 to >60) rather than a continuous measure of EdU+ cells per animal. In this author's opinion, the graph strongly suggests a continuous data set, and the fact that this reviewer had to dig through poorly-labeled raw data to discover the nature of the data is problematic. The authors should either switch to a continuous data set or make it explicit that the data shown are ordinal. If counting EdU+ cells is too arduous, the authors could consider comparing the amount of EdU+ area to the amount of DAPI+ area in maximum intensity projections of their confocal images, as this would roughly approximate the amount of proliferative cells in the animals.

As the reviewer correctly pointed out, the data were treated as ordinal because counting worms with more than 60 Edu+ cells became extremely difficult and highly inaccurate. Therefore, we decided to group in a single category, “60 EdU+ cells”, all worms showing more than 60 EdU+ cells. We have now updated Figure 4 where medians are shown instead of media values, Supplementary Table S5 to provide more comprehensive access to the raw counts, and Supplementary Table S6 to indicate the data for EdU+ cells per worm were considered ordinal. Accordingly, we have revised the corresponding sections as follows:

Results, lines 211 ff.:

“HS-cultured schistosomula showed higher numbers of proliferating stem cells, with a median of >48 and >60 EdU+ cells per worm at days 8 and 15, respectively (Figure 4). On the other hand, most FBS-cultured parasites displayed no more than an average of 20 EdU+ cells per worm (Figure 4).”

Methods, lines 520 ff.:

“EdU+ cells per parasite were counted for an average of 100 parasites across three independent experiments (Supplementary Table S5). Worms were grouped based on the number of cells per individual, but all those showing ⪰ 60 EdU+ cells were counted in the same group named ‘60 EdU+ cells'. Therefore, the data were considered ordinal data. Statistical analysis was performed by Kruskal-Wallis test with Dunn multiple comparison post-hoc test, with P≤0.05 considered significant (Supplementary Table S6).”

Figure 4 legend, lines 830 ff.:

“A. Violin plots showing the number of Edu+ cells per worm at indicated time points (2, 8, and 15 days post cercarial transformation) in parasites cultured either in Foetal Bovine Serum (FBS, blue) or Human Serum (HS, light brown). Human Red Blood Cells (hRBCs) were added in the culture at day 13 post cercarial transformation. The small black dots indicate individual worms, and the big black point indicates the median of EdU+ cells per worm. All worms showing ⪰ 60 EdU+ cells were counted and clustered together in the group named ‘60 EdU+ cells’. Hence, the data were treated as ordinal and statistical analysis performed by Kruskal-Wallis test with Dunn multiple comparison post-hoc test, with P≤0.05 (*) considered significant (Supplementary Tables S5 and S6).”

We thank the reviewer for the very interesting suggestion to quantify cell proliferation by calculating the ratio between EdU+ area to DAPI+ area in maximum intensity projections images. Measuring the fluorescence area for each worm in maximum projection is an excellent idea; however, due to the number of EdU+ cells present in some samples, we think this technique would not provide additional information or produce more detailed data compared with our analysis when the number of Edu+ cells exceeds 60 per worm. We will certainly consider this approximation for future studies.

There are some minor issues as well:

(1) Line 122: It is perhaps incorrect to refer to humans as "the" definitive host of schistosomes, as S. japonicum is primarily considered a zoonotic infection with water buffalo/cows being the primary definitive host.

We thank the reviewer for pointing this out; we have now replaced “schistosomes” with “Schistosoma mansoni” (current line 131)

(2) Line 185/298: The authors refer to EdU pulse-chase experiments, but the experiments described here are EdU pulse experiments.

This is a very good point, we thank the reviewer for bringing this up and have accordingly edited by replacing “EdU pulse-chase” with “EdU pulse” experiments in lines 37, 204, and 321.

Reviewer #3 (Public review):

Summary:

This study is significant as it established a protocol for the long-term culture of Schistosoma mansoni newly transformed cercariae, which developed in vitro into sexually dimorphic forms. The impact of two different sera, Fetal Bovine Serum (FBS) and Human Serum (HS), added to the culture medium supplemented with human red blood cells was evaluated. The authors demonstrated that HS-cultured parasites were able to digest red blood cells, a critical step for long-term parasite development. Furthermore, while most FBS-cultured parasites did not progress beyond an early liver stage, sexual dimorphism was clearly evident in the HS-cultured worms, albeit delayed compared to in vivo development.

Strengths:

This study could contribute to further in vitro studies for a better understanding of the unique sexual biology of Schistosoma mansoni and for screening novel schistosomicidal compounds. By increasing parasite development in in vitro studies, this protocol could have a positive impact on the principles of the 3Rs (Replacement, Reduction and Refinement) for animal research.

We thank the reviewer for highlighting the manuscript’s strengths.

Weaknesses:

As the authors mentioned, "pairing between male and female parasites was rare. Pairing was observed in approximately ~7% of the experiments, usually after day ~ 80 in culture. Egg production was also not achieved with this protocol.

Following the reviewer’s point and to clarify a misleading point, we have now decided to remove the value of 7% — which corresponds to the percentage of experiments in which couples were observed. However, this value does not accurately reflect the actual number of observed worm pairs, and it is probably misleading. We have updated the text as follows:

Results, lines 230 ff.:

“While the establishment of sexual dimorphism was robust and reproducible across more than 15 independent experiments, pairing between male and female parasites was rare. Pairing was observed only in experiments lasting more than 80 days in which we were only able to observe a few couples. In addition, these pairings were temporary (Figures 6A, B; Supplementary Video S4).”

eLife Assessment

In this work, the authors demonstrated that blue light mediated mitochondrial contacts attenuated blue light induced mitochondrial dysfunction, and validated this in human cells and C. elegans. This valuable work has the potential to provide novel perspectives into the field of mitochondrial biology but the supporting data are incomplete.

Reviewer #1 (Public review):

Summary:

Blue light exposure has been shown to induce mitochondrial dysfunction, including reduced mitochondrial membrane potential (MMP). In the present study, the authors present a protein-based optogenetic system capable of inducing mito-contacts upon blue LED illumination, and show that this technical platform attenuated blue-light-induced mitochondrial dysfunction and cytotoxicity via restoring mitochondrial membrane potential.

Strengths:

The overall study design is well organized, and the data appear to support the conclusions. Additionally, demonstrating effects in human retinal cells and C. elegans enhances the perceived robustness and translational potential of the findings.

Weaknesses:

(1) Quantification of MMP at contact sites: The use of Rhodamine 123 (Rh123) for MMP measurement can be problematic, as it is not ratiometric; its signals depend on loading conditions, cell size, mitochondrial mass, and focal thickness, rather than solely on ΔΨm. If mitochondrial content changes (e.g., via biogenesis or mitophagy), Rh123 readings can be misleading. This is particularly relevant here, as the mito-contact-induced MMP changes appear to be localized events. The authors should include controls for at least one experiment using FCCP/CCCP (to collapse ΔΨm) and oligomycin (to induce hyperpolarization in many cell types) to confirm the dynamic range of the assay. Where possible, Rh123 fluorescence intensity should be normalized to mitochondrial mass (e.g., using a mass marker or mitochondrial protein). Moreover, MMP changes should be validated using an alternative indicator, such as JC-1 or a genetically encoded probe, as this is foundational to the study.

(2) Mechanisms of mito-contact-induced MMP hyperpolarization: Building on the above, what is the mechanism by which mito-contacts induce MMP hyperpolarization? Does this involve fusion of the outer or inner mitochondrial membranes? MMP hyperpolarization typically reflects an increase in protons in the intermembrane space relative to the matrix. Where do these protons originate? The kinetics of mito-contact-induced MMP changes should also be investigated in more detail.

(3) Building on the above, what is the ratio of contact area to the overall mitochondrial surface area? If MMP increases only at relatively small contact sites, how does this translate to an overall increase in MMP and energy production?

(4) Blue light causes mitochondrial damage via increased reactive oxygen species (ROS), and MMP hyperpolarization can itself lead to excessive oxidative stress. The authors should measure ROS levels and discuss their potential impact on the observed effects.

(5) Although the main focus is on blue LED-mediated injury, the protective effects of the optogenetic system against other stressors (e.g., ischemia-reperfusion, H₂O₂, or FCCP exposure) should be examined. This would help exclude confounds related to blue light, which is central to both the manipulation and the damage model in the current study, and increase the overall impact of the findings.

Reviewer #2 (Public review):

Summary:

This paper describes a novel tool (CRYO2PHR-MiroTM), which aims to create contact sites between mitochondria. One elegant aspect of the technique is that it is controlled by the exposure of cells to blue-light and reversible when cells are put back in the dark. Through an unknown and unexplored mechanism, the mitochondrial membrane potential is raised at the mitochondrial contact sites. The oligomerization of CRYOPHR-MiroTM is protective against the toxic effect of prolonged blue light exposure in cells and nematodes.

Strengths:

This work might open novel perspectives in the fundamental study of mitochondria.

(1) CRYO2PHR-MiroTM represents an interesting tool to manipulate mitochondria interaction/proximity/distribution without playing with the classical components of the mitochondrial fusion and fission machinery.

(2) This work suggests that, without the need for fusion, the relative proximity of mitochondria might influence their activity, opening novel fields of investigation in mitochondrial biology.

(3) Finally, targeting CRYO2PHR not only to mitochondria but also to their partner organelles (ER, LD, peroxisomes...) could provide a tool to reversibly manipulate the interaction of mitochondria with the rest of the organelle community.

Weaknesses:

As detailed below, the claims made by the author that CRYOPHR induce mitochondrial contact sites are not fully convincing at this stage. The method used to define and analyse contact sites is not clear enough, and the image presented in the present manuscript does not convincingly illustrate contact sites between mitochondria. Finally, the evidence that CRYOPHR does not trigger mitochondrial fusion should be strengthened.

Comments on the results:

(1) The quantification of mitochondrial contacts is a crucial point of this study. At this stage, the data are not sufficient to demonstrate that CRYOPHR-MiroTM oligomerisation tethers mitochondria. CRYOPHR-MiroTM can oligomerise in Trans, leading to mitochondrial tethering, but it can also oligomerise in Cis. In that later case, one could hypothesise that the massive aggregation of CRYOPHR-MiroTM at the mitochondrial outer membrane could locally push lipids away and/or create membrane curvature. The image and quantification provided by the author make it difficult to decide whether CRYOPHR-MiroTM tethers mitochondria or pinches their membranes. Below are detailed comments on these aspects:

a) It is claimed that "the proportion of mitochondria having one or more mito-contacts increased by nearly 50% following optogenetic stimulation". However, it is unclear how the authors have calculated this parameter. In the methods for contact ratio calculation, it is written that "the contacted area of CRY2PHR puncta was calculated", but I do not understand what it means and how it relates to contact ratio calculation. Then the authors have written, "Based on the area or distance (between mitochondria), the mitochondria were classified as either non-contact or contact". It is not clear to which parameter the term " area " refers: the area of mito-contacts based on MitoTracker or the area of CRY2PHR puncta. It is not clear how the authors integrate the two parameters "area" and "distance" to decide whether two mitochondria are in contact or not.

b) The method states that "Contact ratio refers to the number of contact mitochondria by the total number of mitochondria". What does "number of contact mitochondria" mean? The number of contacts between mitochondria? The number of mitochondria in contact? What is the distance range between two mitochondria, taking into account optic resolution, for which the authors consider that two mitochondria are "in contact"?

c) The quantification of the contact ratio made on the TEM picture should be explained.

d) The following data should be added, as contact site formation is a critical point. On cells treated or not with blue light, the author should measure systematically what is the distance of a given mitochondrion to the nearest one. The distribution of these distance values should be shown and analysed to determine whether or not there are more mitochondria at short distances upon blue light induction of CRYOPHR oligomerization. In addition, the author should determine the number of CRYO2PHR puncta that are simply lying on a mitochondrion and the number of CRYO2PHR puncta that are bridging two clear, distinct mitochondria.

e) Based on the images provided in Figure 1, there is no convincing evidence of mitochondrial contacts. In image 1g, the CRYO2PHR puncta seem to be lying on mitochondrial tubules. Sometimes, it looks that CRYO2PHR puncta decorate mitochondrial constriction sites, suggesting that the CRYOPHR might pinch membranes. The authors claim that they "found various types of mitochondrial contacts (Figure 1f, 1g), such as head-to-head, side-by-side, and head-to-side", but it is not clearly visible on the images. One problem is that the authors show the merge of MTDR and CRYOPHR-mCherry staining, in which the mitochondria contact are hidden by very bright CRYOPHR-mCherry aggregates. The authors should provide high magnification images (like in 1g) showing not only the merge of mitochondria and CRYOPHR-mCherry but also the staining of mitochondria by themselves. The authors should mark "head-to-head, side-by-side, and head-to-side contacts" with arrows.

f) Continuing on Figure 1f and 1g, it does not sound optimal to use CRYOPHR-mcCherry in combination with MTDR (MitoTracker Deep Red) to precisely delimitate subtle membrane contact sites between mitochondria because the emission and excitation spectra of these two fluorochromes partially overlap. One better alternative could be to use MTG (MitoTracker Green) as for Figure 1a. However, here we come to the point that MitoTraker stains the mitochondrial matrix that is delimited by the mitochondrial inner membrane, which can be discontinuous in a given mitochondrion. To formally visualise mitochondrial contact sites and demonstrate that CRYOPHR tethers mitochondria, the author should rather mark the mitochondrial outer membrane (with TOM20::GFP and anti-TOM20, for instance).

g) Figure S2 presents snapshots of a movie clearly showing the rapid aggregation of CRYOPHR into distinct puncta upon blue light exposure. The author should perform the same experiment on cells in which mitochondria would be stained with a fluorophore, allowing live imaging (MTG or TOM20::GP, for instance). This would allow for tracking of mitochondria and CRYOPHR puncta at the same time. Hence, high magnification views should allow for capturing events where CRYOPHR puncta formation coincides with mitochondrial tethering if the authors' claims are correct, or with, for instance, membrane pinching if they are wrong.

h) If CRYOPHR-TMMiro bring mitochondrial membrane closer, it would be surprising that it does not increase the probability of Mitofusin-dependent fusion events. The author should conduct analysis of the mitochondrial network in cells exposed to the conditions shown in Figure 1. Rather than relying only on the aspect ratio (as shown in Figure 2 in cells stressed by prolonged blue light exposure), the author should also analyse the mitochondrial total branch length (sum of the length of all branches from a mitochondrion) and the number of branches on each mitochondrion.

i) Ideally, the author should not only rely on the analysis of mitochondrial architecture, which only partially informs on mitochondrial fusion rate. Fragmented mitochondria can indeed fuse efficiently via kiss-and-run events, for instance. To formally demonstrate that there are no permanent nor transcient fusion at the mitochondrial contact sites induced by CRYOPHR, the most powerful method would be to analyse diffusion of matrix fluorescent dyes. This can be conducted using photoconvertible probes (mt-dendra2) (Pham et al., 2012) or a PEG-induced cell fusion assay (Detmer et al., 2007).

(2) Regarding the quantification of local MMP at mitochondrial contact, it would be important to better explain how the authors have set up their microscope to avoid technical issues that could lead to fluorescent artifacts at CRYOPHR puncta. Because the emission of Rhodamine 123 overlaps the excitation of mCherry, it should be explained in the methods how the detection of Rhodamine 123 has been filtered to avoid the detection of the red light coming from the mCherry light coming from CRYOPHR puncta. This is critical as fluorescent protein aggregates can be very bright.

Comments on the introduction and discussion

(1) In the results section, the authors state that they were "Inspired by previous studies indicating that nanoscale proximity of a charged membrane or protein 119 condensate to a membrane amplifies the local membrane potential". It could be useful to the readers to have a bit of background regarding these observations (references 55 and 56) to better understand what supports the rationale of the authors' strategy. Then, the discussion part should address in more detail the possible mechanisms that could explain why bringing the mitochondrial membranes without fusing them influences mitochondrial membrane potential.

(2) I would suggest finding a simple name for the CRYOPHR-MiroTM tool that could evoke more clearly that it is an optogenetic tool designed to tether mitochondria with blue light.

eLife Assessment

This study provides potentially important insights by establishing a human disease model and exploring therapeutic approaches. The evidence is generally convincing for descriptive and comparative findings. The authors present solid data, but evidence for proposed biological mechanisms and functional outcomes remains limited.

Reviewer #1 (Public review):

In this study, the authors set out to develop a human disease model using stem cell-derived systems and to use this platform to investigate disease biology and evaluate potential therapeutic approaches. Their goal is to provide a tractable experimental system that captures key features of the disease and enables testing of candidate interventions.

The work has several important strengths. The authors present a carefully constructed model with improved genetic replication and clearer reporting of biological replicates, which enhances confidence in the reproducibility of the findings. The longitudinal design, spanning early developmental stages to later disease-relevant phenotypes, provides a useful framework for distinguishing temporal aspects of the disease process. The study also includes a comparative evaluation of multiple therapeutic strategies adding practical value to the field. In addition, statistical reporting and transparency have been strengthened, and key limitations of the model-such as the absence of certain cell types-are now clearly acknowledged.

At the same time, notable weaknesses temper the strength of the conclusions. Several central biological claims, particularly those related to specific signaling pathways, are supported primarily by transcriptomic and protein-level observations without direct functional validation. Similarly, measures used to interpret cellular processes do not fully distinguish between alternative biological explanations, leaving some mechanistic interpretations unresolved. The therapeutic findings are supported by biochemical changes, but evidence for functional recovery at the cellular level is limited. These gaps mean that some of the broader conclusions should be interpreted with caution.

Overall, the authors have largely achieved their aim of establishing a useful experimental model and demonstrating its potential for studying disease-related changes and testing interventions. The evidence is convincing for the descriptive and comparative aspects of the work, but more limited for mechanistic and functional claims.

The study is likely to have a meaningful impact by providing a platform that others in the field can build upon. The methods and datasets will be useful to researchers interested in disease modeling and therapeutic development. At the same time, the work is best viewed as an important foundation, with key mechanistic and functional questions remaining to be addressed in future studies.

Reviewer #2 (Public review):

Sun et al. have developed a midbrain-like organoid (MLO) model for neuronopathic Gaucher disease (nGD). The MLOs recapitulate several features of nGD molecular pathology, including reduced GCase activity, sphingolipid accumulation, and impaired dopaminergic neuron development. They also characterize the transcriptome in the MLO nGD model. CRISPR correction of one of the GBA1 mutant alleles rescues most of the nGD molecular phenotypes. The MLO model was further deployed in proof-of-principle studies of investigational nGD therapies, including SapC-DOPS nanovesicles, AAV9-mediated GBA1 gene delivery, and substrate-reduction therapy (GZ452). This patient-specific 3D model provides a new platform for studying nGD mechanisms and accelerating therapy development. Overall, only modest weaknesses are noted, and these have been adequately addressed in the revision.

Comments on revisions:

I have no further recommendations. The revised manuscript addresses the few questions and concerns that I had initially shared.

Reviewer #3 (Public review):

Summary:

In this study, the authors describe modeling of neuronopathic Gaucher disease (nGD) using midbrain-like organoids (MLOs) derived from hiPSCs carrying GBA1 L444P/P415R or L444P/RecNciI variants. These MLOs recapitulate several disease features, including GCase deficiency, reduced enzymatic activity, lipid substrate accumulation, and impaired dopaminergic neuron differentiation. Correction of the GBA1 L444P variant restored GCase activity, normalized lipid metabolism, and rescued dopaminergic neuronal defects, confirming its pathogenic role in the MLO model. The authors further leveraged this system to evaluate therapeutic strategies, including: (i) SapC-DOPS nanovesicles for GCase delivery, (ii) AAV9-mediated GBA1 gene therapy, and (iii) GZ452, a glucosylceramide synthase inhibitor. These treatments reduced lipid accumulation and ameliorated autophagic, lysosomal, and neurodevelopmental abnormalities.

Strengths:

This manuscript demonstrates that nGD patient-derived MLOs can serve as an additional platform for investigating nGD mechanisms and advancing therapeutic development.

Comments on revisions:

I have no further concerns regarding this manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Lin et al. presents a timely, technically strong study that builds patient-specific midbrain-like organoids (MLOs) from hiPSCs carrying clinically relevant GBA1 mutations (L444P/P415R and L444P/RecNcil). The authors comprehensively characterize nGD phenotypes (GCase deficiency, GluCer/GluSph accumulation, altered transcriptome, impaired dopaminergic differentiation), perform CRISPR correction to produce an isogenic line, and test three therapeutic modalities (SapC-DOPS-fGCase nanoparticles, AAV9GBA1, and SRT with GZ452). The model and multi-arm therapeutic evaluation are important advances with clear translational value.

My overall recommendation is that the work undergo a major revision to address the experimental and interpretive gaps listed below.

Strengths:

(1) Human, patient-specific midbrain model: Use of clinically relevant compound heterozygous GBA1 alleles (L444P/P415R and L444P/RecNcil) makes the model highly relevant to human nGD and captures patient genetic context that mouse models often miss.

(2) Robust multi-level phenotyping: Biochemical (GCase activity), lipidomic (GluCer/GluSph by UHPLC-MS/MS), molecular (bulk RNA-seq), and histological (TH/FOXA2, LAMP1, LC3) characterization are thorough and complementary.

(3) Use of isogenic CRISPR correction: Generating an isogenic line (WT/P415R) and demonstrating partial rescue strengthens causal inference that the GBA1 mutation drives many observed phenotypes.

(4) Parallel therapeutic testing in the same human platform: Comparing enzyme delivery (SapC-DOPS-fGCase), gene therapy (AAV9-GBA1), and substrate reduction (GZ452) within the same MLO system is an elegant demonstration of the platform's utility for preclinical evaluation.

(5) Good methodological transparency: Detailed protocols for MLO generation, editing, lipidomics, and assays allow reproducibility

Weaknesses:

(1) Limited genetic and biological replication

(a) Single primary disease line for core mechanistic claims. Most mechanistic data derive from GD2-1260 (L444P/P415R); GD2-10-257 (L444P/RecNcil) appears mainly in therapeutic experiments. Relying primarily on one patient line risks conflating patient-specific variation with general nGD mechanisms.

We thank the reviewer for highlighting the importance of genetic and biological replication. An additional patient-derived iPSC line was included in the manuscript, therefore, our study includes two independent nGD patient-derived iPSC lines, GD2-1260 (GBA1^L444P/P415R) and GD2-10-257 (GBA1^{L444P/RecNcil}), both of which carry the severe mutations associated with nGD. These two lines represent distinct genetic backgrounds and were used to demonstrate the consistency of key disease phenotypes (reduced GCase activity, elevated substrate, impaired dopaminergic neuron differentiation etc.) across different patient’s MLOs. Major experiments (e.g., GCase activity assays, substrate, immunoblotting for DA marker TH, and therapeutic testing with SapC-DOPS-fGCase, AAV9-GBA1) were performed using both patient lines, with results showing consistent phenotypes and therapeutic responses (see Figs. 2-6, and Supplementary Figs. 4-5). To ensure clarity and transparency, a new Supplementary Table 2 summarizes the characterization of both, the GD2-1260 and GD2-10-257 lines.

(b) Unclear biological replicate strategy. It is not always explicit how many independent differentiations and organoid batches were used (biological replicates vs. technical fields of view).

Biological replication was ensured in our study by conducting experiments in at least 3 independent differentiations per line, and technical replicates (multiple organoids/fields per batch) were averaged accordingly. We have clarified biological replicates and differentiation in the figure legends.

(c) A significant disadvantage of employing brain organoids is the heterogeneity during induction and potential low reproducibility. In this study, it is unclear how many independent differentiation batches were evaluated and, for each test (for example, immunofluorescent stain and bulk RNA-seq), how many organoids from each group were used. Please add a statement accordingly and show replicates to verify consistency in the supplementary data.

In the revision, we have clarified biological replicates and differentiation in the figure legend in Fig.1E; Fig.2B,2G; Fig.3F, 3G; Fig.4B-C,E,H-J, M-N; Fig.6D; and Fig.7A-C, I.

(d) Isogenic correction is partial. The corrected line is WT/P415R (single-allele correction); residual P415R complicates the interpretation of "full" rescue and leaves open whether the remaining pathology is due to incomplete correction or clonal/epigenetic effects.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was not feasible because GBA1 overlaps with a highly homologous pseudogene (PGBA), which makes precise editing technically challenging. Consequently, only the L444P mutation was successfully corrected, and the resulting isogenic line retains the P415R mutation in a heterozygous state. Because Gaucher disease is an autosomal recessive disorder, individuals carrying a single GBA1 mutation (heterozygous carriers) do not develop clinical symptoms. Therefore, the partially corrected isogenic line, which retains only the P415R allele, represents a clinically relevant carrier model. Consistent with this, our results show that GCase activity was restored to approximately 50% of wild-type levels (Fig.4B-C), supporting the expected heterozygous state. These findings also make it unlikely that the remaining differences observed are due to clonal variation or epigenetic effects.

(e) The authors tested week 3, 4, 8, 15, and 28 old organoids in different settings. However, systematic markers of maturation should be analyzed, and different maturation stages should be compared, for example, comparing week 8 organoids to week 28 organoids, with immunofluorescent marker staining and bulk RNAseq.

We agree that a systematic analysis of maturation stages is essential for validating the MLO model. Our data integrated a longitudinal comparison across multiple developmental windows (Weeks 3 to 28) to characterize the transition from progenitors to mature/functional states for nGD phenotyping and evaluation of therapeutic modalities: 1) DA differentiation (Wks 3 and 8 in Fig. 3): qPCR analysis demonstrated the progression of DA-specific programs. We observed a steady increase in the mature DA neuron marker TH and ASCL1. This was accompanied by a gradual decrease in early floor plate/progenitor markers FOXA2 and PLZF, indicating a successful differentiation path from progenitors to differentiated/mature DA neurons. 2) Glycosphingolipid substrates accumulation (Wks 15 and 28 in Fig 2): To assess late-stage nGD phenotyping, we compared GluCer and GluSph at Week 15 and Week 28. This comparison highlights the progressive accumulation of substrates in nGD MLOs, reflecting the metabolic consequences of the disease at different mature stage. 3) Organoid growth dynamics (Wks 4, 8, and 15 in new Fig. 4): The new Fig. 4 tracks physical maturation through organoid size and growth rates across three key time points, providing a macro-scale verification of consistent development between WT and nGD groups. By comparing these early (Wk 3-8) and late (Wk 15-28) stages, we confirmed that our MLOs transition from a proliferative state to a post-mitotic, specialized neuronal state, satisfied the requirement for comparing distinct maturation stages.

(f) The manuscript frequently refers to Wnt signaling dysregulation as a major finding. However, experimental validation is limited to transcriptomic data. Functional tests, such as the use of Wnt agonist/inhibitor, are needed to support this claim (see below).

We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work.

(g) Suggested fixes / experiments

Add at least one more independent disease hiPSC line (or show expanded analysis from GD2-10-257) for key mechanistic endpoints (lipid accumulation, transcriptomics, DA markers).

Additional line iPSC GD2-10-257 derived MLO was included in the manuscript. This was addressed above [see response to Weaknesses (1)-a].

Generate and analyze a fully corrected isogenic WT/WT clone (or a P415R-only line) if feasible; at minimum, acknowledge this limitation more explicitly and soften claims.

We attempted to generate an isogenic iPSC line by correcting both GBA1 mutations (L444P and P415R). However, this was unsuccessful because the GBA1 gene overlaps with a pseudogene (PGBA) located16kd downstream of GBA1, which shares 9698% sequence similarity with GBA1) (Ref#1, #2), which complicates precise editing. GBA1 is shorter (~5.7 kb) than PGBA (~7.6 kb). The primary exonic difference between GBA1 and PGBA is a 55-bp deletion in exon 9 of the pseudogene. As a result, the isogenic line we obtained carries only the P415R mutation, and L444P was corrected to normal sequence. We have included this limitation in the Methods as “This gene editing strategy is expected to also target the GBA1 pseudogene due to the identical target sequence, which limits the gene correction on certain mutations (e.g., P415R)”.

References:

(1) Horowitz M., Wilder S., Horowitz Z., Reiner O., Gelbart T., Beutler E. The human glucocerebrosidase gene and pseudogene: structure and evolution. Genomics (1989). 4, 87–96. doi:10.1016/0888-7543(89)90319-4

(2) Woo EG, Tayebi N, Sidransky E. Next-Generation Sequencing Analysis of GBA1: The Challenge of Detecting Complex Recombinant Alleles. Front Genet. (2021). 12:684067. doi: 10.3389/fgene.2021.684067. PMCID: PMC8255797.

Report and increase independent differentiations (N = biological replicates) and present per-differentiation summary statistics.

This was addressed above [see response to Weaknesses (1)-b, (1)-c].

(2) Mechanistic validation is insufficient

(a) RNA-seq pathways (Wnt, mTOR, lysosome) are not functionally probed. The manuscript shows pathway enrichment and some protein markers (p-4E-BP1) but lacks perturbation/rescue experiments to link these pathways causally to the DA phenotype.

(b) Autophagy analysis lacks flux assays. LC3-II and LAMP1 are informative, but without flux assays (e.g., bafilomycin A1 or chloroquine), one cannot distinguish increased autophagosome formation from decreased clearance.

(c) Dopaminergic dysfunction is superficially assessed. Dopamine in the medium and TH protein are shown, but no neuronal electrophysiology, synaptic marker co-localization, or viability measures are provided to demonstrate functional recovery after therapy.

(d) Suggested fixes / experiments - Perform targeted functional assays:

(i) Wnt reporter assays (TOP/FOP flash) and/or treat organoids with Wnt agonists/antagonists to test whether Wnt modulation rescues DA differentiation.

(ii) Test mTOR pathway causality using mTOR inhibitors (e.g., rapamycin) or 4E-BP1 perturbation and assay effects on DA markers and autophagy.

Include autophagy flux assessment (LC3 turnover with bafilomycin), and measure cathepsin activity where relevant.

Add at least one functional neuronal readout: calcium imaging, MEA recordings, or synaptic marker quantification (e.g., SYN1, PSD95) together with TH colocalization.

We thank the reviewer for these valuable suggestions. We agree that the suggested experiments could provide additional mechanistic insights into this study and will consider them in future work. Importantly, the primary conclusions of our manuscript, that GBA1 mutations in nGD MLOs resulted in nGD pathologies such as diminished enzymatic function, accumulation of lipid substrates, widespread transcriptomic changes, and impaired dopaminergic neuron differentiation, which can be corrected by several therapeutic strategies in this study, are supported by the evidence presented. The suggested experiments represent an important direction for future research using brain organoids.

(3) Therapeutic evaluation needs greater depth and standardization

(a) Short windows and limited durability data. SapC-DOPS and AAV9 experiments range from 48 hours to 3 weeks; longer follow-up is needed to assess durability and whether biochemical rescue translates into restored neuronal function.

We agree with the reviewer. Because this is a proof-of-principle study, the treatment was designed within a short time window. Long-term studies with more comprehensive outcome assessments will be conducted in future work.

(b) Dose-response and biodistribution are under-characterized. AAV injection sites/volumes are described, but transduction efficiency, vg copies per organoid, cell-type tropism quantification, and SapC-DOPS penetration/distribution are not rigorously quantified.

We appreciate the reviewer’s concerns. This study was intended to demonstrate the feasibility and initial response of MLOs to AAV therapy. A comprehensive evaluation of AAV biodistribution will be considered in future studies.

The penetration and distribution of SapC-DOPS have been extensively characterized in prior studies. In vivo biodistribution of SapC–DOPS coupled CellVue Maroon, a fluorescent cargo, was examined in mice bearing human tumor xenografts using real-time fluorescence imaging, where CellVue Maroon fluorescence in tumor remained for 48 hours (Ref. #3: Fig. 4B, mouse 1), 100 hours (Ref. #4: Fig. 5), up to 216 hours (Ref. #5: Fig. 3). Uptake kinetics were also demonstrated in cells, with flow cytometry quantification showing that fluorescent cargo coupled SapC-DOPS nanovesicles, were incorporated into human brain tumor cell membranes within minutes and remained stably incorporated into the cells for up to one hour (Ref. # 6: Fig. 1a and Fig. 1b). Building on these findings, the present study focuses on evaluating the restoration of GCase function rather than reexamining biodistribution and uptake kinetics.

References:

(3) X. Qi, Z. Chu, Y.Y. Mahller, K.F. Stringer, D.P. Witte, T.P. Cripe. Cancer-selective targeting and cytotoxicity by liposomal-coupled lysosomal saposin C protein. Clin. Cancer Res. (2009) 15, 5840-5851. PMID: 19737950.

(4) Z. Chu, S. Abu-Baker, M.B. Palascak, S.A. Ahmad, R.S. Franco, and X. Qi. Targeting and cytotoxicity of SapC-DOPS nanovesicles in pancreatic cancer. PLOS ONE (2013) 8, e75507. PMID: 24124494.

(5) Z. Chu, K. LaSance, V.M. Blanco, C-H. Kwon, B. Kaur, M. Frederick, S. Thornton, L. Lemen, and X. Qi. Multi-angle rotational optical imaging of brain tumors and arthritis using fluorescent SapC-DOPS nanovesicles. J. Vis. Exp. (2014) 87, e51187, 1-7. PMID: 24837630.

(6) J. Wojton, Z. Chu, C-H. Kwon, L.M.L. Chow, M. Palascak, R. Franco, T. Bourdeau, S. Thornton, B. Kaur, and X. Qi. Systemic delivery of SapC-DOPS has antiangiogenic and antitumor effects against glioblastoma. Mol. Ther. (2013) 21, 1517-1525. PMID: 23732993.

(c) Specificity controls are missing. For SapC-DOPS, inclusion of a non-functional enzyme control (or heat-inactivated fGCase) would rule out non-specific nanoparticle effects. For AAV, assessment of off-target expression and potential cytotoxicity is needed.

Including inactive fGCase would confound the assessment of fGCase in MLOs by immunoblot and immunofluorescence; therefore, saposin C–DOPS was used as the control instead.

We agree that assessment of off-target expression and potential cytotoxicity for AAV is important, this will be included in future studies.

(d) Comparative efficacy lacking. It remains unclear which modality is most effective in the long term and in which cellular compartments.

To address this comment, we have added a new table (Supplementary Table 2) comparing the four therapeutic modalities and summarizing their respective outcomes. While this study focused on short-term responses as a proof-of-principle, future work will explore long-term therapeutic effects.

(e) Suggested fixes/experiments

Extend follow-up (e.g., 6+ weeks) after AAV/SapC dosing and evaluate DA markers, electrophysiology, and lipid levels over time.

We appreciate the reviewer’s suggestions. The therapeutic testing in patient-derived MLOs was designed as a proof-of-principle study to demonstrate feasibility and the primary response (rescue of GCase function) to the treatment. A comprehensive, long-term therapeutic evaluation of AAV and SapC-DOPS-fGCase is indeed important for a complete assessment; however, this represents a separate therapeutic study and is beyond the scope of the current work.

Quantify AAV transduction by qPCR for vector genomes and by cell-type quantification of GFP+ cells (neurons vs astrocytes vs progenitors).

For the AAV-treated experiments, we agree that measuring AAV copy number and GFP expression would provide additional information. However, the primary goal of this study was to demonstrate the key therapeutic outcome, rescue of GCase function by AAV-delivered normal GCase, which is directly relevant to the treatment objective.

Include SapC-DOPS control nanoparticles loaded with an inert protein and/or fluorescent cargo quantitation to show distribution and uptake kinetics.

As noted above [see response to Weakness (3)-c], using inert GCase would confound the assessment of fGCase uptake in MLOs; therefore, it was not suitable for this study. See response above for the distribution and uptake kinetics of SapC-DOPS [see response to Weaknesses (3)-b].

Provide head-to-head comparative graphs (activity, lipid clearance, DA restoration, and durability) with statistical tests.

We have added a new table (Supplementary Table 2) providing a head-to-head comparison of the treatment effects.

(4) Model limitations not fully accounted for in interpretation

(a) Absence of microglia and vasculature limits recapitulation of neuroinflammatory responses and drug penetration, both of which are important in nGD. These absences could explain incomplete phenotypic rescues and must be emphasized when drawing conclusions about therapeutic translation.

We agree that the absence of microglia and vasculature in midbrain-like organoids represents a limitation, as we have discussed in the manuscript. In this revision, we highlighted this limitation in the Discussion section and clarified that it may contribute to incomplete phenotyping and phenotypic rescue observed in our therapeutic experiments. Additionally, we have outlined future directions to incorporate microglia and vascularization into the organoid system to better recapitulate the in vivo environment and improve translational relevance (see 7th paragraph in the Discussion).

(b) Developmental vs degenerative phenotype conflation. Many phenotypes appear during differentiation (patterning defects). The manuscript sometimes interprets these as degenerative mechanisms; the distinction must be clarified.

We appreciate the reviewer’s comments. In the revised manuscript, we have clarified that certain abnormalities, such as patterning defects observed during early differentiation, likely reflect developmental consequences of GBA1 mutations rather than degenerative processes. Conversely, phenotypes such as substrate accumulation, lysosomal dysfunction, and impaired dopaminergic maturation at later stages are interpreted as degenerative features. We have updated the Results and Discussion sections to avoid conflating developmental defects with neurodegenerative mechanisms.

(c) Suggested fixes

Tone down the language throughout (Abstract/Results/Discussion) to avoid overstatement that MLOs fully recapitulate nGD neuropathology.

The manuscript has been revised to avoid overstatements.

Add plans or pilot data (if available) for microglia incorporation or vascularization to indicate how future work will address these gaps.

The manuscript now includes further plans to address the incorporation of microglia and vascularization, described in the last two paragraphs in the Discussion. Pilot study of microglia incorporation will be reported when it is completed.

(5) Statistical and presentation issues

(a) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

We have clarified biological replicates and differentiation in the figure legend [see response to Weaknesses (1)-b, (1)-c].

(b) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

We have updated Statistical analysis in methods as described below:

For comparisons between two groups, data were analyzed using unpaired two-tailed Student’s t-tests when the sample size was ≥6 per group and normality was confirmed by the Shapiro-Wilk test. When the normality assumption was not met or when sample sizes were small (n < 6), the non-parametric Mann-Whitney U test was used instead. For comparisons involving three or more groups, one-way ANOVA followed by Tukey’s multiple comparison test was applied when data were normally distributed; otherwise, the nonparametric Dunn’s multiple comparison test was used. Exclusion of outliers was made based on cutoffs of the mean ±2 standard deviations. All statistical analyses were performed using GraphPad Prism 10 software. Exact p-values are reported throughout the manuscript and figures where feasible. A p-value < 0.05 was considered statistically significant.

(c) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

In this work, quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM. This multilevel averaging approach minimizes bias from regional heterogeneity within organoids and accounts for variability across differentiations. Representative confocal images shown in the figures were selected to accurately reflect the quantified data. We believe this standardized quantification strategy ensures robust and reproducible results while appropriately representing the 3D architecture of the organoids.

In the revision, we have clarified the method used for image analysis of sectioned MLOs as below:

Quantitative immunofluorescence analyses (e.g., cell counts for FOXP1+, FOXG1+, SOX2+ and Ki67+ cells, as well as marker colocalization) were performed using ImageJ (NIH) on at least 3–5 randomly selected non-overlapping fields of view (FOVs) per organoid section, with a minimum of 3 organoids per differentiation batch. Each FOV was imaged at consistent magnification (60x) and z-stack depth to ensure comparable sampling across conditions. Data from individual FOVs were first averaged within each organoid to obtain an organoid-level mean, and then biological replicates (independent differentiations, n ≥ 3) were averaged to generate the final group mean ± SEM.

(d) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

RNA-seq data are from same batch. The mapping rate is >90%. GEO accession will be active upon publication. These were included in the Methods.

(e) Suggested fixes

Add a table summarizing biological replicates, technical replicates, and statistical tests used for each figure panel.

We have revised the figure legends to include replicates for each figure and statistical tests [see response in weaknesses (1)-b, (1)-c].

Recompute statistics where appropriate (non-parametric if N is small) and report effect sizes and confidence intervals.

Statistical analysis method is provided in the revision [see response in Weaknesses (5)-b].

(6) Minor comments and clarifications

(a) The authors should validate midbrain identity further with additional regional markers (EN1, OTX2) and show absence/low expression of forebrain markers (FOXG1) across replicates.

We validated the MLO identity by 1) FOXG1 and 2) EN1. FOXG1 was barely detectable in Wk8 75.1_MLO but highly present in ‘age-matched’ cerebral organoid (CO), suggesting our culturing method is midbrain region-oriented. In nGD MLO, FOXG1 expression is significantly higher than 75.1_MLO, indicating that there was aberrant anterior-posterior brain specification, consistent with the transcriptomic dysregulation observed in our RNA-seq data.

To further confirm midbrain identity, we examined the expression of EN1, an established midbrain-specific marker. Quantitative RT-PCR analysis demonstrated that EN1 expression increased progressively during differentiation in both WT-75.1 and nGD2-1260 MLOs at weeks 3 and 8 (Author response image 1). EN1 reached 34-fold and 373-fold higher levels than in WT-75.1 iPSCs at weeks 3 and 8, respectively, in WT-75.1 MLOs. In nGD MLOs, although EN1 expression showed a modest reduction at week 8, the levels were not significantly different from those observed in age-matched WT-75.1 MLOs (p > 0.05, ns).

Author response image 1.

qRT-PCR quantification of midbrain progenitor marker EN1 expression in WT-75.1 and GD2-1260 MLOs at Wk3 and Wk8. Data was normalized to WT-75.1 hiPSC cells and presented as mean ± SEM (n = 3-4 MLOs per group). ns, not significant.

(b) Extracellular dopamine ELISA should be complemented with intracellular dopamine or TH+ neuron counts normalized per organoid or per total neurons.

We quantified TH expression at both the mRNA level (Fig. 3F) and the protein level (Fig. 3G/H) from whole-organoid lysates, which provides a more consistent and integrative measure across samples. These TH expression levels correlated well with the corresponding extracellular (medium) dopamine concentrations for each genotype. In contrast, TH⁺ neuron counts may not reliably reflect total cellular dopamine levels because the number of cells captured on each organoid section varies substantially, making normalization difficult. Measuring intracellular dopamine is an alternative approach that will be considered in future studies.

(c) For CRISPR editing: the authors should report off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus. (off-target analysis (GUIDE-seq or targeted sequencing of predicted off-targets) or at least in-silico off-target score and sequencing coverage of the edited locus).

The off-target effect was analyzed during gene editing and the chance to target other off-targets is low due to low off-target scores ranked based on the MIT Specificity Score analysis. The related method was also updated as stated below:

“The chance to target other off-targets is low due to low off-target scores ranked based on the MIT Specificity Score analysis (Hsu, P., Scott, D., Weinstein, J. et al. DNA targeting specificity of RNA-guided Cas9 nucleases. Nat Biotechnol 31, 827–832 (2013). https://doi.org/10.1038/nbt.2647).”

(d) It should be clarified as to whether lipidomics normalization is to total protein per organoid or per cell, and include representative LC-MS chromatograms or method QC.

The normalization was to the protein of organoid lysate. This was clarified in the Methods section in the revision as stated below:

“The GluCer and GluSph levels in MLO were normalized to total MLO protein (mg) that were used for glycosphingolipids analyses. Protein mass was determined by BCA assay and glycosphingolipid was expressed as pmol/mg protein. Additionally, GluSph levels in the culture medium were quantified and normalized to the medium volume (pmol/mL).”

Representative LC-MS chromatograms for both normal and GD MLOs have been included in a new figure, Supplementary Figure 2.

(e) Figure legends should be improved in order to state the number of organoids, the number of differentiations, and the exact statistical tests used (including multiplecomparison corrections).

This was addressed above [see response to Weaknesses (1)-b and (5)-b].

(f) In the title, the authors state "reveal disease mechanisms", but the studies mainly exhibit functional changes. They should consider toning down the statement.

The title was revised to: Patient-Specific Midbrain Organoids with CRISPR Correction Recapitulate Neuronopathic Gaucher Disease Phenotypes and Enable Evaluation of Novel Therapies

(7) Recommendations

This reviewer recommends a major revision. The manuscript presents substantial novelty and strong potential impact but requires additional experimental validation and clearer, more conservative interpretation. Key items to address are:

(a) Strengthening genetic and biological replication (additional lines or replicate differentiations).

This was addressed above [see response to Weaknesses (1)-a, (1)-b, (1)-c].

(b) Adding functional mechanistic validation for major pathways (Wnt/mTOR/autophagy) and providing autophagy flux data.

(c) Including at least one neuronal functional readout (calcium imaging/MEA/patch) to demonstrate functional rescue.

As addressed above [see response to Weaknesses (2)], the suggested experiments in b) and c) would provide additional insights into this study and we will consider them in future work.

(d) Deepening therapeutic characterization (dose, biodistribution, durability) and including specificity controls.

This was addressed above [see response to Weaknesses (3)-a to e].

(e) Improving statistical reporting and explicitly stating biological replicate structure.

This was addressed above [see response to Weaknesses (1)-b, (5)-b].

Reviewer #2 (Public review):

Sun et al. have developed a midbrain-like organoid (MLO) model for neuronopathic Gaucher disease (nGD). The MLOs recapitulate several features of nGD molecular pathology, including reduced GCase activity, sphingolipid accumulation, and impaired dopaminergic neuron development. They also characterize the transcriptome in the MLO nGD model. CRISPR correction of one of the GBA1 mutant alleles rescues most of the nGD molecular phenotypes. The MLO model was further deployed in proof-of-principle studies of investigational nGD therapies, including SapC-DOPS nanovesicles, AAV9-mediated GBA1 gene delivery, and substrate-reduction therapy (GZ452). This patient-specific 3D model provides a new platform for studying nGD mechanisms and accelerating therapy development. Overall, only modest weaknesses are noted.

We thank the reviewer for the supportive remarks.

Reviewer #3 (Public review):

Summary:

In this study, the authors describe modeling of neuronopathic Gaucher disease (nGD) using midbrain-like organoids (MLOs) derived from hiPSCs carrying GBA1 L444P/P415R or L444P/RecNciI variants. These MLOs recapitulate several disease features, including GCase deficiency, reduced enzymatic activity, lipid substrate accumulation, and impaired dopaminergic neuron differentiation. Correction of the GBA1 L444P variant restored GCase activity, normalized lipid metabolism, and rescued dopaminergic neuronal defects, confirming its pathogenic role in the MLO model. The authors further leveraged this system to evaluate therapeutic strategies, including: (i) SapC-DOPS nanovesicles for GCase delivery, (ii) AAV9-mediated GBA1 gene therapy, and (iii) GZ452, a glucosylceramide synthase inhibitor. These treatments reduced lipid accumulation and ameliorated autophagic, lysosomal, and neurodevelopmental abnormalities.

Strengths:

This manuscript demonstrates that nGD patient-derived MLOs can serve as an additional platform for investigating nGD mechanisms and advancing therapeutic development.

Comments:

(1) It is interesting that GBA1 L444P/P415R MLOs show defects in midbrain patterning and dopaminergic neuron differentiation (Figure 3). One might wonder whether these abnormalities are specific to the combination of L444P and P415R variants or represent a general consequence of GBA1 loss. Do GBA1 L444P/RecNciI (GD2-10-257) MLOs also exhibit similar defects?

We observed reduced dopaminergic neuron marker TH expression in GBA1 L444P/RecNciI (GD2-10-257) MLOs, suggesting that this line also exhibits defects in dopaminergic neuron differentiation. These data are provided in a new Supplementary Fig. 4E, and are summarized in new Supplementary Table 2 in the revision.

(2) In Supplementary Figure 3, the authors examined GCase localization in SapC-DOPSfGCase-treated nGD MLOs. These data indicate that GCase is delivered to TH⁺ neurons, GFAP⁺ glia, and various other unidentified cell types. In fruit flies, the GBA1 ortholog, Gba1b, is only expressed in glia (PMID: 35857503; 35961319). Neuronally produced GluCer is transferred to glia for GBA1-mediated degradation. These findings raise an important question: in wild-type MLOs, which cell type(s) normally express GBA1? Are they dopaminergic neurons, astrocytes, or other cell types?

All cell types in wild-type MLOs are expected to express GBA1, as it is a housekeeping gene broadly expressed across neurons, astrocytes, and other brain cell types. Its lysosomal function is essential for cellular homeostasis and is therefore not restricted to any specific lineage. (https://www.proteinatlas.org/ENSG00000177628GBA1/brain/midbrain).

(3) The authors may consider switching Figures 2 and 3 so that the differentiation defects observed in nGD MLOs (Figure 3) are presented before the analysis of other phenotypic abnormalities, including the various transcriptional changes (Figure 2).

We appreciate the reviewer’s suggestion; however, we respectfully prefer to retain the current order of Figures 2 and 3, as we believe this structure provides the clearest narrative flow. Figure 2 establishes the core biochemical hallmarks: reduced GCase activity, substrate accumulation, and global transcriptomic dysregulation (1,429 DEGs enriched in neural development, WNT signaling, and lysosomal pathways), which together provide essential molecular context for studying the specific cellular differentiation defects presented in Figure 3. Presenting the broader disease landscape first creates a coherent mechanistic link to the subsequent analyses of midbrain patterning and dopaminergic neuron impairment.

To enhance readability, we have added a brief transitional sentence at the start of the Figure 3 paragraph: “Building on the molecular and transcriptomic hallmarks of GCase deficiency observed in nGD MLOs (Figure 2), we next investigated the impact on midbrain patterning and dopaminergic neuron differentiation (Figure 3).”

Recommendations for the authors:

Reviewing Editor Comments:

Your paper has been reviewed by three expert reviewers in the GBA field. Although they appreciate the work and its novelty, they raise several concerns. We suggest that you to address these concerns in the next version.

Reviewer #1 (Recommendations for the authors):

Statistical and presentation issues

(1) Missing or unclear sample sizes (n). For organoid-level assays, report the number of organoids and the number of independent differentiations.

This was addressed above [see response to Reviewer 1 Weaknesses (1)- b].

(2) Statistical assumptions not justified. Tests assume normality; where sample sizes are small, consider non-parametric tests and report exact p-values.

We have updated methods to describe the Statistical analysis details [see response to Reviewer 1 Weaknesses (5)-b].

(3) Quantification scope. Many image quantifications appear to be from selected fields of view, which are then averaged across organoids and differentiations.

This was addressed above [see response to Reviewer 1 Weaknesses (5)- c].

(4) RNA-seq QC and deposition. Provide mapping rates, batch correction details, and ensure the GEO accession is active. Include these in Methods/Supplement.

Our RNA-seq data were generated from a single batch of MLOs, with mapping rates exceeding 90%. The GEO accession will be made publicly available upon publication.

Reviewer #2 (Recommendations for the authors):

Please consider the following suggestions for revisions:

(1) Line 86: A bit more explanation/justification for the focus on midbrain-like organoids would be helpful, including introducing the nature of the midbrain pathology to better put some of the MLO findings in context. Is the nGD pathology for the midbrain significantly different / out of proportion to other affected brain regions?

nGD Patients often display impaired vertical gaze and movement disorders. These symptoms correlate with midbrain involvement due to the sensitivity of this region to neuroinflammatory and degenerative processes (Ref #7, #8). Both human and mouse studies indicate that the midbrain exhibits prominent substrate accumulation compared to other brain regions, suggesting a predisposition for greater pathological involvement in GD midbrain (Ref #8, #9, #10, #11). This rationale was added to Line 86 in the revision.

References:

(7) Goker-Alpan O, Ivanova MM. Neuronopathic Gaucher disease: Rare in the West, common in the East. J Inherit Metab Dis.(2024) 47(5):917-934. PMID: 38768609.

(8) Burrow TA, Sun Y, Prada CE, Bailey L, Zhang W, Brewer A, Wu SW, Setchell KDR, Witte D, Cohen MB, Grabowski GA. CNS, lung, and lymph node involvement in Gaucher disease type 3 after 11 years of therapy: clinical, histopathologic, and biochemical findings. Mol Genet Metab. (2015) 114(2):233-241. PMID: 25219293.

(9) Tamar Farfel-Becker, Einat B. Vitner, Samuel L. Kelly, Jessica R. Bame, Jingjing Duan, Vera Shinder, Alfred H. Merrill, Kostantin Dobrenis, Anthony H. Futerman. Neuronal accumulation of glucosylceramide in a mouse model of neuronopathic Gaucher disease leads to neurodegeneration, Human Molecular Genetics, (2014). Volume 23, Issue 4, Pages 843–854.

(10) E. Ellen Jones, Wujuan Zhang, Xueheng Zhao, Cristine Quiason , Stephanie Dale, Sheerin Shahidi-Latham, Gregory A. Grabowski, Kenneth D. R. Setchell, Richard R. Drake, and Ying Sun. High-Resolution MALDI Imaging Mass Spectrometry. SLAS Discovery (2017). Vol. 22(10) 1218–1228

(11) Xu YH, Xu K, Sun Y, Liou B, Quinn B, Li RH, Xue L, Zhang W, Setchell KD, Witte D, Grabowski GA. Multiple pathogenic proteins implicated in neuronopathic Gaucher disease mice. Hum Mol Genet. (2014) 23(15):3943-57. PMID: 24599400.

(2) Lines 359-360: Please specify the carbon-chain length of the sphingoid base of the GluCer species analyzed. Also, is there a citation for the statement that 18:0 and 16:0 are "brain-enriched species"?

The carbon-chain length analyzed ranges from 14:0 to 24:0. The sphingoid base for all GluCer species analyzed is d18:1. For example, the species referred to as GluCer 18:0 corresponds to GluCer(d18:1/18:0). Although both, 16:0 and 18:0 are enriched in the brain, 18:0 is the most abundant species in the brain (Ref #12, #13). We revised "brain-enriched species” to “brain-predominant species (18:0)”.

References:

(12) Nilsson, O., and Svennerholm, L. Accumulation of Glucosylceramide and Glucosylsphingosine (Psychosine) in Cerebrum and Cerebellum in Infantile and Juvenile Gaucher Disease. Journal of Neurochemistry (1982) 39, 709–718.

(13) Sun, Y., Zhang, W., Xu, Y.H., Quinn, B., Dasgupta, N., Liou, B., Setchell, K.D., and Grabowski, G.A. Substrate compositional variation with tissue/region and Gba1 mutations in mouse models--implications for Gaucher disease. PLoS One (2013). 8, e57560.10.1371/journal.pone.0057560.

(3) Figure 2: It would be interesting to compare the MLO findings to prior gene expression data. Are there previously published transcriptome analyses from nGD brain tissue (or other tissues) that the transcriptome data obtained from MLOs may be compared with? What about transcriptome analyses of mouse GD models?

We thank the reviewer for this valuable suggestion. To strengthen the biological context of our transcriptomic findings, we have added a new comparative table (new Supplementary Table 3) in the revised manuscript that summarizes key dysregulated pathways in our human nGD MLOs alongside previously published data from nGD mouse midbrain (Ref#14). The table highlights substantial overlap, including axon guidance, neuron differentiation, dopaminergic/glutamatergic/GABAergic synaptic signaling, lipid metabolism, apoptosis/cell death, and nervous system development, emphasizing the translational relevance of our model. We also note that our dataset uniquely reveals pronounced dysregulation of WNT signaling and anterior-posterior patterning (Fig. 2L and 2M), potentially reflecting human-specific early midbrain defects.

We added the following sentence to Discussion: “Comparative analysis with prior transcriptomic data from nGD mouse midbrain showed consistent dysregulation in axon guidance, synaptic signaling, lipid metabolism, and nervous system development (new Supplementary Table 3), supporting the fidelity of our human MLO model.”

Reference:

(14) Dasgupta N, Xu YH, Li R, Peng Y, Pandey MK, Tinch SL, Liou B, Inskeep V, Zhang W, Setchell KD, Keddache M, Grabowski GA, Sun Y. Neuronopathic Gaucher disease: dysregulated mRNAs and miRNAs in brain pathogenesis and effects of pharmacologic chaperone treatment in a mouse model. Hum Mol Genet. (2015) 24(24):7031-48. PMID: 26420838.

(4) Lines 402-405 & Figure 3D: Is it possible to include a merged image to better visualize the TH and FOXA2 co-staining / potential colocalization?

The merged images of TH (red) and FOXA2 (green) are shown in Fig. 3E. Yellow arrows indicate TH and FOXA2 co-stained cells, which appear yellow in the merged images. The results demonstrate that the number of co-stained cells is reduced in GD2-1260 MLOs compared with WT-75.1 MLOs at both, week 6 and week 8.

(5) Lines 447-448 & Figure 4F, G, J: It would be helpful to provide a direct analysis/visualization of MLO size between the WT-75.1, GD2-1260, and iso-GD2-1260 genotypes (allowing direct comparison of WT and iso). Similarly, the same 3-way analysis would be valuable for assessing dopamine levels.

We have included WT-75.1 in Fig. 4 F/G/J in the revision. All three genotypes, WT-75.1, GD2-1260, and iso-GD2-1260, are presented for analysis compared to WT-75.1. In new Figure 4F, MLO growth is presented by representative MLO images taken under wide field microscopy at day 2, Wk4 and Wk8 of differentiation. In new Fig. 4G, MLOs size was analyzed by NIS elements and presented as the area (µm²) of MLO in image (mean ± SEM). N≥10 MLOs were analyzed for each genotype. In new Fig. 4J. Dopamine levels in MLO culture medium from WT-75.1, GD2-1260 and iso- GD2-1260 MLOs at Wk12 cultured in 3 mL BGM medium for 72 hours were analyzed. Data are presented as mean ± SEM (n = 5 per group). Statistical analysis applied was described in the legend.

(6) Figure 4: What is the explanation/interpretation of the residual autophagy pathway dysfunction in CRISPR-corrected MLOs? nGD requires near-complete loss of GCase activity, so it is a bit curious that autophagic dysfunction would be observed with only ~50% GCase reduction? There is some discussion, but it doesn't fully capture the unexpected nature and implications of this result.

This phenomenon may be explained by a threshold effect in lysosomal function. Gaucher disease is an autosomal recessive disorder. The carriers with heterozygous GBA1 mutation, who retain approximately 50% of normal GCase activity, do not develop disease. This suggests that even partial restoration of GCase activity can reduce glucosylceramide accumulation below a pathological threshold, thereby restoring lysosomal integrity and autophagic flux. In addition, improved GCase activity may help normalize the lipid composition of lysosomal membranes, facilitating the fusion events required for effective autophagy.

(7) Lines 512-516 & Figure 5J: The data shown are inconclusive. Can these Western blot data be quantified, noting the number of replicates for each measurement? Without quantification and statistics, it is difficult to assess the claim that levels of LAMP1, LC3-I, LC3-II, 4E-BP1, and p-4E-BP1 in GD2-1260 treated with SapC-DOPS-fGCase are more similar to GD2-1260 treated following SapC-DOPS than to WT-75.1.

We performed quantitative analysis by comparing WT-75.1 and included the data in new Fig. 5J. The result was revised as:

Analysis of protein levels showed that decreased LAMP1 expression in GD2 1260 MLOs was not altered following SapC DOPS fGCase treatment (Figure 5J). The elevated LC3-II levels, an indicator of impaired autophagic flux, were reduced upon treatment, suggesting enhanced autophagic activity (Figure 5J). Moreover, phosphorylated 4E-BP1 (Thr37/46), but not total 4E-BP1, was improved in SapC-DOPS-fGCase–treated MLOs, reflecting a decrease in mTOR hyperactivation (Figure 5J). We anticipate that a longer duration of SapC-DOPS-fGCase exposure in nGD MLOs may produce a more robust therapeutic effect in rescuing nGD-associated phenotypes, which will be evaluated in future studies.

(8) Lines 518-520: The presented data support "effective restoration of GCase activity," but clarification is needed regarding "correction of GD-related disease phenotypes." Perhaps "selected molecular and biochemical phenotypes" would be more accurate. Data are not shown for several other phenotypes, including TH, FOXA2, and dopamine levels.

This was revised to “selected molecular and biochemical phenotypes “.

(9) Figure 5D-J: Please clarify whether all experiments were conducted 48 hours after treatment, as indicated for Figure 5C. If so, does this suggest that SapC-DOPS treatment exhibits only short-term effects? Were any data collected to evaluate the persistence of the treatment effect?

The treatment duration is specified in the Fig. 5 legend. Fig. 5D–J represent experiments conducted after two weeks of treatment, whereas Fig. 5C reflects a 48-hour treatment. In both Gaucher disease lines, two-week treatment restored GCase activity to wild-type levels and reduced GluSph substrate accumulation. These findings were intended as proof-of-principle to demonstrate therapeutic feasibility; evaluation of treatment persistence beyond two weeks was beyond the scope of this study.

Minor suggestions

(1) Line 80: "A brain organoid derived from hiPSCs of a healthy individual with GBA1 knockout and α-synuclein overexpression exhibited some PD features23." I would suggest enumerating what "PD features" are to distinguish from "clinical features", which I don't think is the intended meaning.

This was revised as “exhibited characteristic PD markers”.

(2) Figure 2I: The reported number of downregulated DEGs is incorrect. It should be 765, not 1429.

This was corrected in Figure 2I.

(3) Line 359: change "enrich" to "enriched".

This word was corrected.

eLife Assessment

This study presents a valuable methodological contribution exploiting the DEER background decay to quantify supramolecular packing in amyloid fibrils. The evidence is incomplete: the observation of D < 1 is inconsistent with the theoretical lower bound of the model, and it remains unclear whether this reflects a genuine systematic limitation or falls within experimental uncertainty.