Author response:

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

Reviewer #1 (Public review):

Summary:

The authors present a novel approach to subcellular spatial proteomics by combining laser microdissection with expansion microscopy and LC-MS/MS analysis (SPEx). They implement two different workflows for LMD and LC-MS/MS quantification:

(1)The standard approach, where an area of interest is cut out by LMD, subjected to proteomics analysis, and compared to the rest of the cell without the dissected ROI.

(2) The subtraction approach, where ROIs are removed, and the remaining cellular material is compared to samples containing both the surrounding material and the ROI.

The authors assess the technique by applying it to subcellular targets of various sizes, volumes, and protein compositions such as the nucleus, nucleoli, and Golgi. They demonstrate that SPEx can identify proteins enriched or reduced in ROIs.

Strengths:

The broad, relatively easy, and inexpensive applicability of this approach to potentially many cell types and subcellular areas of interest provides an exciting alternative to subcellular fractionation, native immunoprecipitation, or genetically encoded proximity labeling constructs. Moreover, by visually selecting ROIs for subsequent analysis, subcellular context or organelle morphology can be taken into account, as discussed by the authors in the discussion section.

Weaknesses:

While strongly supporting the sharing of this approach, we have a number of comments and questions that will improve the impact of the manuscript:

We thank the reviewer for the careful evaluation of our manuscript and the generally positive assessment.

(1) General:

(a) The manuscript would benefit from restructuring and language revision. In its current form, the writing is sometimes dense and verbose (in particular, the Results section). This makes it difficult to follow the authors' arguments.

We improved readability and clarity in the revised manuscript. We added subheadings to facilitate reading.

(b) The authors mention the possibility of selecting organelles based on morphology. This is left for the discussion, but it seems like a missed opportunity - the authors could compare individual organelles in different morphological states, e.g., connected vs. fragmented mitochondria.

The authors agree with the reviewers’ assessment that investigating proteome of organelles based on morphology or cellular state is an exciting application of SPEx. While we plan experiments along this line in the future, we think that these experiments are beyond the scope of this manuscript, which is meant to describe the method and its general usefulness.

(2) Technical:

(a) Why do the authors strive and optimize for a 10x expansion factor? Is SPEx compatible with a more standard 4x expansion, as e.g., used in the classic U-ExM approach (https://www.nature.com/articles/s41592-018-0238-1)? This could be added to the discussion.

We aimed for 10x expansion solely because our ultimate goal is to cut out very small structures. 10x expansion results in a 100x increase in area, while in U-ExM the area increase would only by 16x. Thus, this makes a huge difference for small structures such as nucleoli. We did not assess the compatibility with U-ExM. Still, we performed pilots with just 4x expansion (using TREx) in the early stages of optimization. We were able to isolate single cells and obtain similar protein coverage as with 10x expansion. We further clarified our motivation to use 10x expansion in the discussion.

(b) The U-ExM approach shows improved ultrastructural preservation when using 3%FA with 0.1% glutaraldehyde fixation (GA). Is SPEx compatible with the use of low amounts of GA for fixation?

We tried different fixation methods in the early stages of this study (where expansion was not yet close to 10x). We saw a mild negative effect of GA on the expansion factor, so we avoided it in the later experiments since it also did not seem necessary to preserve the structure of our organelles of interest. However, the use of GA would generally be compatible with SPEx, potentially at the cost of a mild negative effect on expansion factor (see Author response image 1) and proteome coverage. We discussed the use of GA in the discussion section.

Author response image 1.

Fixation methods mini-screen. Cells were fixed with the indicated reagents for 10 minutes at 37°C. After TREx expansion, the diameter of the nucleus was measured (A) and the resulting expansion factor compared to the non-expanded control was determined (B).

Related to the above, was the anchoring efficiency reduced only to achieve a 10x expansion factor or does this additionally affect the proteome coverage?

We solely lowered the anchoring to increase expansion factors. In earlier pilots we performed proteomic analysis on samples that were just expanded 4x using standard TREx expansion (also using the original anchoring strategy from the TREx publication, consisting of 0.2 mg/ml AcX for overnight at RT). We presented the results of this pilot in Fig S1A. We still detected over 2,000 proteins from 10 cells, a coverage, which is highly similar to what we found in the final experiments (Figure 2F), in which the anchoring was lower for 10x expansion. Based on these data, we think that anchoring (and expansion factor!) has a negligible impact on protein coverage. We clarified this point in the manuscript.

(d) Have the authors considered using alternative anchoring approaches, such as GMA (https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0291506#pone.0291506.s001), which potentially increase the amount of sample retained in the hydrogel, thus allowing for better proteome coverage? This could be added to the discussion.

We did not use alternative anchoring approaches. We modified the TREx protocol to fit our purposes and since this was sufficient, we did not explore alternatives. However, using anchoring approaches, in which higher amounts of sample could be retained in the gel might be beneficial for the proteomics coverage. We will keep this suggestion in mind for future experiments. Thank you for the suggestion!

(e) The limitation of the approach to near-2D samples should be mentioned, and alternative approaches for more 3D samples could be discussed.

The authors agree that SPEx is limited to near-2D samples at this point. We suggest that SPEx is applicable for 3D samples (e.g. in tissues) by performing cryosectioning. TREx has been shown to be compatible with sectioned tissue (Damstra et al., 2022). We discuss this point in the discussion.

(f) How are peptides that are directly anchored to the hydrogel dealt with during LC-MS/MS analysis? Are they excluded, or can they be identified during the spectral search? The latter would allow us to get a deeper structural understanding of how proteins are actually anchored into hydrogels, which so far has not been assessed.

The reviewer raises an interesting point. In general, peptides carrying the anchoring modification are analysed by LC-MS, but we did not include these specific modifications in the database search. Overall, we assumed that the labeling would be low and stochastic and hence should, if at all, only minimally affect the detection of peptides. Nevertheless, in response to the reviewers’ comment, we searched the MS data again for the crosslinking reagent linked to lysine residues. However, we could not get any confident hit for any peptide containing this modification. Since we cannot exclude that the modification precludes the identification of the corresponding peptides, we compared the number peptides generated by trypsin cleavage after arginine and lysine. As the human genome contains similar proportions of both amino acids, one would expect similar numbers for both peptide types being identified. Any modifications of lysine by the anchoring reagent, would prevent tryptic cleavage and thus reduce the number of lysine peptides. As shown in Figure S1C, the number of lysine-terminating is only slightly lower compared to arginine-terminating peptides. Notably, the proteomics results of a different fixed human tissue sample directly extracted by laser capture micro dissection without expansion showed a very similar lysine-to-arginine peptide ratio. This indicates that the large majority of lysine residues is not modified and affected by the hydrogel anchoring. We included these data into the manuscript.

An alternative approach to address this question would be to investigate if the peptide coverage of proteins detected by SPEx is enriched for peptides representing the folded core of proteins as opposed to the surface-exposed regions, which likely get more anchored into the hydrogel.

Because of the negligible amounts of modified peptides, we did not investigate this potential bias of surface-exposed versus folded-core peptides.

(g) Same question regarding peptides with NHS labeling. Can they be identified, or do they just compete for ionization and thus negatively affect coverage and dynamic range of the LC-MS/MS approach?

The reviewer raises a similar point as above for another lysine labeling used during the SPEx protocol. Again, we specifically looked for this modification by re-searching the raw MS data, but still could not identify any peptides, carrying this modification on a lysine residue. Even though we cannot exclude that this rather large modification prevents detection, considering the high number of lysine-terminating peptides in our dataset (see Figure S1 C), we would expect that also this labeling step is stochastic and affects only a minor proportion of the proteins. We discuss the potential NHS labeling in the manuscript.

(h) How are the primary and secondary antibodies affecting the proteomics analysis identified as contaminants?

We thank the reviewer for this comment. Since antibodies bind to proteins in a non-covalent manner, they will be released during the denaturing steps of the protocol. Of course, the antibodies will stay in the sample, be digested and analyzed and could, if very abundant, affect the analysis of the proteins from the samples. To check this possibility, we re-searched the MS data including the sequences of the antibodies used. To our surprise, we could not detect any peptides of these antibodies. This suggests that the concentrations of the antibodies used are much lower than those of the sample proteins and thus should not have any impact on the proteomics results. We interpret this result also as a benefit of our method compared to organellar-IP.

(i) Have the authors observed differences in proteomics coverage of only antibody vs NHS-labeling? Depending on the questions above, could pure antibody-based labeling increase proteomic coverage?

We did not perform this comparative analysis, since we always used NHS dyes. In the experiments presented in this manuscript, NHS dyes allowed easy visualization of the whole cell without the use of antibodies. This NHS staining was essential for this particular setup for sample acquisition. We cut out entire cells, cells lacking the nucleus and cells lacking the Golgi apparatus, which served as critical controls. However, other ways of detecting cell boundaries could be used to avoid NHS staining. As shown above, both, the anchor and NHS labeling are likewise sparse and stochastic. Moreover, we could not detect any impact of the antibody labeling to our results. Thus, we assume that both labeling procedures could be used.

Reviewer #1 (Recommendations for the authors):

(1) Introduce the aberration PPS-membrane.

We apologize for the omission and now explain the PPS abbreviation.

(2) Please state which cells are used already in the first section "Development of the SPEx method" as opposed to only further down in the manuscript.

We apologize for the omission, which has been fixed.

(3) In Figures 2D and E, the authors should also show the hydrated expansion factors for better comparison.

We agree that the inclusion of the hydrated expanded gels allows for better comparison. These data are now included in the manuscript.

Reviewer #2 (Public review):

Summary:

This study introduces a method that combines physical expansion of cells, imaging-guided isolation of defined regions, and protein identification to enable compartment-resolved analysis of protein composition at the subcellular scale. The authors aim to address a central limitation in existing approaches, namely the loss of spatial information during sample preparation or the indirect nature of proximity-based labeling methods. Using several cellular compartments as examples, they demonstrate that their approach can recover compartment-enriched protein sets and identify candidate proteins with previously unassigned localization.

Strengths:

A major strength of this work is the conceptual simplicity and accessibility of the approach. By combining established techniques in a modular way, the method avoids the need for genetic manipulation or specialized labeling strategies, making it broadly adaptable across experimental systems. The ability to directly select regions of interest based on imaging represents a clear advantage over indirect enrichment strategies and allows flexible targeting of both membrane-bound and non-membrane-bound compartments.

The experimental design is also a strong aspect of the study. The use of complementary comparison strategies-analyzing isolated compartments alongside matched "subtracted" controls-provides an internal framework for assessing enrichment and depletion, increasing confidence in spatial assignment. The application of the method across multiple organelles of different sizes and properties demonstrates versatility, and the reported specificity for several compartments is encouraging. In particular, the ability to profile small and biochemically challenging structures highlights a potentially important niche for the approach.

Weaknesses:

Despite these strengths, several methodological limitations constrain the interpretation of the results. The most important relates to spatial accuracy in three dimensions. While lateral resolution is improved through physical expansion, the lack of depth resolution introduces uncertainty regarding contributions from structures above and below the selected region. Although the authors argue that this does not substantially affect specificity, the current evidence is largely indirect, and a more rigorous quantification of potential contamination would strengthen this conclusion.

Quantitative interpretation also remains challenging. Because the measurements reflect total protein abundance rather than local concentration, differences in compartment size and protein density can influence enrichment values, particularly for small structures embedded within larger volumes. This issue is evident in the analysis of smaller compartments and complicates direct comparison across conditions. Additional normalization or modeling would help clarify how to interpret these measurements.

Another limitation concerns variability in the expansion process and its downstream consequences. Differences in expansion factor across samples may affect the definition of regions of interest and introduce variability in sampling, yet the impact of this variability is not fully explored. Similarly, the use of a modified chemical treatment to preserve proteins for downstream analysis is central to the workflow but is not extensively validated with respect to preservation of spatial organization.

While the identification of previously unannotated proteins is an appealing aspect of the study, validation is limited to a small number of examples, and broader support from independent datasets or literature context is lacking. In addition, the study primarily focuses on steady-state measurements in a single cell type, and therefore does not yet demonstrate the ability of the method to capture dynamic or condition-dependent changes in protein localization.

Finally, the positioning of the method relative to existing approaches could be more clearly articulated. Although qualitative comparisons are provided, a more systematic and quantitative benchmarking against alternative strategies would help readers better understand the specific advantages and trade-offs.

We thank the reviewer for the careful evaluation of the manuscript and for the constructive feedback. The reviewer raises valid points, which we addressed in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

Additional experiments and analyses

(1) To strengthen confidence in the spatial specificity of the method, the authors should include experiments or analyses that directly estimate potential cross-compartment contamination. For example, using markers that are known to localize to mutually exclusive cellular regions would allow an empirical assessment of signal carryover. Alternatively, a computational or geometric model could be used to estimate how much material from adjacent regions is expected to contribute to the sampled proteome, given the loss of depth information.

We agree with the reviewer’s concern regarding spatial resolution and potential contaminations resulting from it. We had the same concerns. We have obviously no resolution in z and we detected about 700 proteins (Fig. 5F) in our all samples, likely representing proteins residing above and below of (and potentially next to) the structures we cut out. To overcome this issue, we always compare the proteome of the structure of interest with an appropriate control. We also determined that mitochondria proteins are specifically omitted from our nuclear samples. Moreover, we provide evidence that our analysis methods can be used also to determine proteins that are specifically lost from a structure. Omitting the comparative approach would clearly result in very low specificity and a high number of false positives. However, we argue that comparison to a control largely removes these unspecific contaminations and we think that this is illustrated by our excellent specificity. Nevertheless, to address these concerns further, we have determined the masses of all quantified proteins using iBAQ values. We then summed the masses of all proteins being annotated to a specific organelle and calculated the percentage to the summed masses of all quantified proteins. As expected, we found that in our excised nuclei samples, 75.5% of the protein molecules originate from the nucleus and only 24.5% of protein mass was derived from other regions. Likewise, we found 84.7% of the protein mass in the excised Golgi samples annotated with Golgi or extracellular by GO. This analysis revealed that we detect an expected amount of contaminant proteins derived from other compartments due to the lack of resolution in z, but most of protein mass excised is already organelle-specific. The additional quantification step further enhances assignment accuracy, boosting the overall specificity of our approach. In the case of the nucleoli the mass contribution from known nucleoli proteins is significantly lower (~4%), which would be expected for a structure that only covers a fraction of the cell in z-direction. In the case of such small targets comparison to a fitting control is therefore essential. We added this analysis to the revised version of the manuscript and discuss it in detail (see “SPEx is best used as a comparative approach”). We thank the reviewer for bringing this up!

(2) Given that drying results in compression along the vertical axis while largely preserving the lateral dimensions, it would be valuable to provide a quantitative analysis of how this affects spatial accuracy. This could include comparing marker distributions before and after drying or examining signal distribution across depth.

Even though we were unable to image a particular cell before and after drying (due to the physical properties of the gels and the change in size during drying), we did so for the bulk of cells. We did not observe discernible morphological alterations after drying. The investigated structures (Golgi, nucleus and nucleoli) still looked morphologically similar to expanded cells (before drying) and non-expanded cells. We cannot exclude that the drying process introduced minor distortions of the sample. We would like to point out, however, that our focus is mainly on the spatial proteomics and to a lesser extent on the perfect conservation of the ultrastructure during drying. As long as we can maintain very good spatial separation and are able to cut out individual structures, our method should work just fine.

In addition, trimming or sectioning the expanded samples along the z-axis prior to microdissection could help minimize contributions from structures above and below the region of interest, thereby improving spatial specificity.

We tried to cut expanded samples (monolayer of cells) with a microtome prior to laser dissection. This approach did unfortunately not work. Mounting a monolayer of cells for microtome cutting is non-trivial!  The very thin monolayer of cells would need to be perfectly aligned with the plane where the cryo-sectioning takes place. Moreover, the different densities of the hydrogel without cells and the expanded cells in the same hydrogel appeared to be particular challenging during sectioning. Therefore, we gave up on this approach for monolayers. For a monolayer of cells, the contamination in the lateral dimension seems to be small enough so it can be eliminated by comparing the sample to appropriate controls, preventing the need for cryo-sectioning. We do think, however, that cryo-sectioning should be feasible for tissues since the combination of cryo-sectioning and TREx expansion in tissues has been described previously (Damstra et al., 2022).

(3) Because the method relies on imaging-guided spatial dissection of a three-dimensional structure, further validation of spatial precision would strengthen the manuscript. Applying z-stack trimming to reduce depth-related ambiguity and comparing results obtained with more conservative and spatially restricted cutting boundaries would help determine how sensitive the proteomic output is to segmentation strategy and provide a clearer assessment of robustness.

As pointed out above, we were unable to perform trimming in z. Therefore, the proposed analysis cannot be performed.

(4) The use of SDS-based denaturation instead of protease digestion represents a key methodological deviation from conventional expansion workflows and is central to enabling downstream proteomic analysis. The authors should provide additional validation demonstrating that this approach preserves spatial fidelity without introducing distortion or bias in protein localization.

We respectfully disagree with the reviewer. SDS denaturation was used previously in both the TREx and the U-ExM protocols (Damstra et al., 2022; Gambarotto et al., 2021). The preservation of ultrastructure has been established in both studies. Still, as pointed out by the reviewer, protease digestion is frequently used in ExM, likely because it minimizes distortion of the sample by eliminating any mechanical resistance to expansion. We omitted protease treatment to be able to perform LC-MS/MS. Protease treatment would likely reduce the amounts of peptides we would be able to detect. However, with the extended SDS denaturation, we were able to maintain excellent expansion even in the absence of protease treatment.

(5) The manuscript reports variability in expansion factors across conditions, and it would be important to more clearly establish reproducibility. The authors should quantify variability across biological replicates and discuss how differences in expansion factor influence region-of-interest selection, spatial resolution, and downstream quantitative analysis.

We were surprised that this reviewer thinks that we have variability in the expansion factors across conditions. In fact, the expansion is rather reproducible, and we only observe very minor variability in expansion factors between samples. The minor differences in expansion factor are unlikely to affect sampling because sampling happens manually and differences in the size of an organelle are accounted for by just adjusting the size of the isolated ROI. Even if we would have some discernible difference in the expansion factor between samples, this would not matter. The organelle of interest is cut out from the same cell, which will be subsequently used as control. Each sample subjected to LC-MS/MS contained at least 10 individually cut-out objects, further eliminating variability potentially introduced by minor changes in expansion levels.

(6) The authors should also address how differences in compartment size and protein density influence quantitative interpretation. Because proteomic measurements reflect total protein abundance rather than local concentration, smaller compartments may be underrepresented. Incorporating normalization strategies or simulations would help clarify how enrichment values should be interpreted across compartments.

We agree with the reviewer that comparison of structures of very different sizes might be technically difficult and that in such cases, controls should be collected in a similar size range to the actually studied compartments. We have implemented this change already in our workflow and mention this consideration in the discussion.

Regarding normalization, we employed median normalization to our proteomics data abundances which controls for different sample amounts and eventually results in a comparison of protein concentration rather than pure protein abundances. This approach eliminates any knowledge of cell or organelle size and allows a more uniform comparison. We do agree, however, with the reviewer that for differential proteomics analysis, regions of interest should be preferable of the similar size and protein amount to avoid normalization biases. We discussed this point in the revised manuscript.

(7) Validation of newly identified compartment-associated proteins should be expanded. In particular, the interpretation of proteins such as C7orf50 and SPOUT1 would benefit from deeper contextual discussion, including whether prior studies have reported alternative localizations under different cellular conditions and whether their localization may be cell-type-specific or context-dependent.

We agree that more contextual discussion of the newly localized proteins will benefit the manuscript. We added more information about the newly identified proteins to the results section.

(8) To support broader claims about the utility of the method, the authors should consider demonstrating that the approach can capture biologically meaningful, context-dependent changes in protein localization. For example, comparing different cell types or applying defined perturbations such as stress or apoptosis would help establish the ability of the method to resolve dynamic intracellular remodeling.  

The authors agree with the reviewers’ assessment that studying context-dependent changes at a subcellular level is an exciting idea to explore. While we are currently planning such experiments, we think that these experiments are beyond the scope of this manuscript, which is meant to describe the method and its general usefulness.

(9) The manuscript would benefit from a more direct and quantitative comparison with existing spatial proteomics approaches. In particular, benchmarking against proximity labeling methods would help clarify relative performance in terms of specificity and false positive rates, and comparison with published datasets could provide an objective frame of reference.

We are a bit puzzled by the reviewer’s request. We already compared SPEx to a number of established spatial proteomics methods in the paper (Figure S1I-J, Figure S2F-G, Figure 5F-G) and discuss coverage and specificity. However, we expanded this comparison further to methods using Exm combined with LMD in the new manuscript (see below).

(10) In addition, the positioning of the method relative to other expansion-based spatial proteomics approaches remains insufficiently defined. The authors are encouraged to include a structured comparison, ideally in the form of a summary table, outlining key parameters such as sampling strategy, spatial resolution, proteome depth, spatial specificity, throughput, and limitations. This would help clearly delineate the unique contributions of the approach within the broader methodological landscape.

Peer reviewer’s request, we added a table (S15) on spatial proteomics methods combining expansion microscopy with manual or laser dissection and also provide information about lateral resolution, sampling strategy, proteome coverage, advantages and limitations.

Writing and presentation

(1) The presentation of expansion-related measurements would benefit from clearer organization. Currently, expansion factors from non-dried and dried samples are presented in separate figures, which may create redundancy and confusion. Reorganizing these data to directly compare pre- and post-drying conditions, or moving non-essential measurements to supplementary material, would improve clarity.

We now also show the hydrated expansion factors in Figure 2C-D for comparison.

(2) The method used for quantifying expansion should be described more explicitly. It should be clarified whether the same structures were tracked before and after expansion or whether independent samples were used, particularly for nuclei, which vary in size.

We use the nucleus because this also used by other groups in the field (Liffner et al., 2024). The tracked structures are from independent samples. Thus, we average over a number of structures and calculate the expansion factor based on the mean diameter. We made this clearer in the manuscript.

(3) Additional clarification is needed regarding the fluorescent labeling strategy. The rationale for using different dyes across experiments should be explained to distinguish whether these choices are driven by technical constraints, experimental design, or visualization preferences.

We agree with the reviewer that the manuscript will profit from a more in-depth discussion of the labeling strategy. The structure of interest was always labeled in red because in our hands more red-shifted dyes are more resistant to drying than e.g. green dyes. We added this information to the manuscript.

(4) Several figure legends and result descriptions would benefit from revision for clarity and completeness. In particular, complex panels such as intersection analyses should be more fully explained to ensure accessibility to readers.

We agree with the reviewer’s assessment. The intersection analysis and the PCA, which represent the most complex panels in the manuscript, are now more clearly described in the legends.

(5) The authors should also improve clarity in describing structural changes associated with drying. Including representative images of gels before and after drying would help illustrate the preservation of lateral dimensions and compression along the vertical axis.

We agree that this addition would improve the manuscript. We included the images as Figure S1B. The gel post-drying is outlined by black dots because the gels become very thin and near-invisible post-drying.

Minor corrections

(1) Minor issues should be addressed to improve consistency and readability. These include correcting figure cross-references, standardizing statistical notation throughout the manuscript, and resolving typographical inconsistencies.

Done.

(2) Specific figure-related issues should also be addressed, including clarifying mislabeled figure references and improving color schemes in plots where group distinctions are currently difficult to interpret.

Done.

Data and reproducibility

(1) The authors should ensure that all datasets and analysis workflows are fully accessible and sufficiently documented to enable reproducibility. This includes providing raw and processed proteomics data, as well as detailed descriptions of analysis pipelines and parameter settings.

Raw proteomics data for all experiments will be publicly available upon publication of the final version and workflows are described in a detailed manner. To improve reproducibility, we also included a step-by-step explanation of the assembly of the gelation chamber, which represents the handling-wise most challenging step of the protocol, in Figure S3D.

Reviewer #3 (Public review):

Franziscus et al. describe an elegant approach for spatially specific proteome analysis. To achieve this, they expand fixed cells and subsequently use a laser to micro-dissect a region of interest, which is then analyzed by mass spectrometry.

They demonstrate the effectiveness of their approach by analyzing the nucleus, nucleolus, and the Golgi, and benchmark their hits against previous datasets for these organelles.

The manuscript is very well written and nicely guides the reader through the applied methods. The presented data is convincing, and I do not see the need for additional experimental verification of the protocol. The only minor concern is the novelty of the method and the presentation. A combination of expansion, laser microdissection, and proteomics has been applied in the past (PMID: 36450705, PMID: 39477916). In the manuscript, one of these studies is cited, though it does not become clear that this approach is already described. However, Franziscus et al. describe the approach better and make it more accessible to the reader, especially since the other studies described this methodology in combination with tissue expansion and not in combination with single cell expansion as it is done here. I would ask the authors to be clearer in the introduction about what others have already done and what their contribution is here. In general, I am convinced that the community will benefit from the presented protocol to analyze organelle proteomics in detail.

We thank the reviewer for the careful evaluation of our manuscript and overwhelmingly positive assessment. We apologize for the omission of the mentioned citations, which are now included in the manuscript together with a direct comparison with the mentioned methods (Table S15).

References

Damstra HG, Mohar B, Eddison M, Akhmanova A, Kapitein LC, Tillberg PW. 2022. Visualizing cellular and tissue ultrastructure using Ten-fold Robust Expansion Microscopy (TREx). eLife 11:e73775. DOI: https://doi.org/10.7554/eLife.73775

Gambarotto D, Hamel V, Guichard P. 2021. Ultrastructure expansion microscopy (U-ExM). Methods in Cell Biology 161:57–81. DOI: https://doi.org/10.1016/bs.mcb.2020.05.006, PMID: 33478697

Liffner B, Silva TLA e., Vega-Rodriguez J, Absalon S. 2024. Mosquito Tissue Ultrastructure-Expansion Microscopy (MoTissU-ExM) enables ultrastructural and anatomical analysis of malaria parasites and their mosquito. BMC Methods 1:13. DOI: https://doi.org/10.1186/s44330-024-00013-4

Author response:

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

eLife Assessment:

This important study identifies and characterizes a set of amino acid states that can rescue protein function in the presence of substantially deleterious mutations. Some of these super-compensatory substitutions also confer substantial mutational robustness, with broader implications for understanding epistasis, protein evolution, and protein engineering. The evidence is convincing, supported by a creative reanalysis of a large deep-mutational-scanning dataset, statistically rigorous treatment of anticipated error rates, experimental validation, and analyses of additional proteins, although clearer presentation and deeper investigation of the evolutionary implications and structural mechanisms would further strengthen the study.

We sincerely thank the Reviewing Editor, the Senior Editor, and the three reviewers for this assessment. The two directions identified in it are addressed directly in the present revision. The structural mechanism of super compensation is now examined with an inverse-folding model in addition to the Rosetta calculations (Reviewer #2, Comment 1); the evolutionary implications are tested on a phylogeny rather than by co-occurrence among extant species, with the remaining limitations stated explicitly (Reviewer #2, Comment 3); and the presentation is revised throughout, including the title, the terminology used for fitness landscapes, the two section titles, the numbering of equations, and the figures (Reviewer #1). We hope that these revisions strengthen the clarity and the evolutionary interpretation of the study.

Reviewer #1 (Public review):

Summary:

The study identifies and characterizes a set of amino acid states that make the protein robust to other mutations, to the point of being able to compensate mutations that render wildtype proteins entirely non-functional. The study uses a previously published dataset and uses it to find and study such super-compensators. It then analyzes the biophysics and fitness landscape structure of what may be behind the compensation, identifying stability as an important parameter that, nevertheless, is not sufficient to explain all of the compensatory effect. These findings have important implications for our understanding of protein evolution, with these super-compensators possibly acting in a role of "permissive mutations" and opening up evolutionary trajectories that may be closed without them. Perhaps the identification of such super-compensator substitutions can be incorporated into various protein design approaches.

Strengths:

The paper presents a compelling case with a rigorous analysis of the expected error rates of observation. While not unique, the current state-of-the-art in the field typically does include experimental error rate estimation like this work. The paper also does a good job in exploring the issue, including looking at plausible biophysical basis of super-compensators.

We are deeply grateful to Reviewer #1 for the constructive feedback and the careful reading of our manuscript. We are particularly encouraged by the assessment that the paper “presents a compelling case with a rigorous analysis” of the expected error rates of observation, and by the recognition that the identification of super compensatory substitutions may inform protein design approaches. The comments on the rigor of the evolutionary framing, on the presentation of the fitness-potential analysis, and on the figures were highly valuable in improving the manuscript. We have carefully considered each point and itemize the corresponding revisions below.

Weaknesses:

(1) The paper lacks rigor in talking about evolutionary-related issues of the state of the fitness landscape. As an example, the paper mentions that these super-compensators flatten the landscape. While I understand where this is coming from, I think that the fitness landscape in this context is a static entity and cannot be flattened or otherwise altered. A much more accurate description is that a sequence with a super-compensator is located in a flatter-than-expected segment of the fitness landscape, or on a flat fitness ridge. These issues are more semantic in nature, and while the manuscript would benefit from it being shown to an expert in molecular evolution or fitness landscapes, this issue does not take away from the importance of the results.

We thank the reviewer for the suggestions. The proposed title is “Super-compensatory substitutions restore protein function and confer local mutational robustness”. The replacement text distinguishes the fixed genotype-to-fitness map from comparisons among local neighborhoods within that map. “Local mutational robustness” is defined operationally as a smaller absolute measured effect of the same second-site substitution in matched backgrounds carrying the focal state. The prepared prose removes statements that a substitution “flattens,” “smooths,” or changes the landscape and instead says that a genotype occupies a locally flatter region or fitness ridge.

Reviewer #1 (Recommendations for the authors):

I think that there should be more rigor when talking about or painting a mental picture of the fitness landscape (see above). More minor comments below:

Main text

(1) Line 106: "pooled competitive growth assays" -> is it correct to call it "competitive"? By design, there should not be competition in the sense that the presence or absence of cells with genotype A should not influence the growth rate of cells with genotype B.

We thank the reviewer for the careful terminology check. We fully agree that “competitive” is misleading here, as the assay does not measure direct competition between genotypes. We have revised the term to “pooled growth assays” throughout the manuscript to more accurately reflect the experimental design.

(2) Line 125: 3,750 rescuable genotypes are identified among 31,701 lethal ones (Line 111), but in the abstract the claim is one-third of non-functional missense variants are rescuable (Line 26-27). I am not sure I understand.

We thank the reviewer for catching this inconsistency. Upon re‑checking, we realize that 3,750/31,701 is approximately 11.8% (roughly one‑tenth), not one‑third. The “one‑third” figure in the Abstract was a misstatement and has been corrected to reflect the correct proportion. All other numbers in the main text and abstract have been cross‑checked and are consistent.

(3) Line 149: add citation to His3p being a homo-24-mer.

We thank the reviewer for the suggestion. The citation has been added accordingly (Rawson et al., 2018).

(4) Lines 178-187: I understood the paragraph about the fitness potential of super compensators, but I think that it should be shown to someone who does not think of fitness potentials as much as I do and see if it makes sense to them.

Please refer to the question 2 of reviewer 3

(5) Line 188: The title (and the paragraph) could focus on buffering beneficial ones; for deleterious, it is given by definition (although strictly only for lethals).

We thank the reviewer for the suggestion. We have revised the title to “Super Compensators Buffer the Effects of Beneficial Substitutions” to clearly emphasize that our study focuses on the buffering of beneficial mutations

(6) Line 238-239: Even more strongly than previously, the title is describing a property given by definition of (super) compensators, is it not?

We thank the reviewer for this critical and insightful point. We fully agree that the original title, “Super Compensators Enhance Organisms’ Tolerance to Deleterious Mutations,” risked stating a tautological property inherent to the definition of compensators. To address this, we revised it to “Validating Super Compensators as Robust Buffers of Deleterious Substitutions”, which now emphasizes the experimental validation aspect rather than a definitional property.

(7) Line 260: Regarding the robustness of the findings in other datasets - first, I did not see any results based on these datasets (maybe that is for another publication), and it is not clear which results are being referred to. Is it the existence of super-compensatory mutations, or their prevalence or their global stabilizing effect, or all of that?

We thank the reviewer for this important query. We have now clarified in the revised manuscript that our analysis of the other datasets was intended to test whether supercompensators can be detected in other proteins, not to estimate their global stabilizing effects. The results (Fig. S7A–B) show that such high‑compensation amino acid states do exist in other systems.

(8) Figure 1A: why does it jump in the diagram from WT 2 mutations away rather than 1?

We thank the reviewer for pointing out the inconsistency in Figure 1A. We have revised the figure as suggested, and the updated version now properly shows the stepwise progression from WT through the single‑mutation intermediate to the double‑mutation state, removing the original jump.

(9) Lines 655-656: Figure 1C dark blue vs black is hard to read.

We thank the reviewer for this suggestion. We have changed the dark blue to light blue in Figure 1C to enhance readability ‘

(10) Figure 2D: given axes, it would read better if it is a square.

We thank the reviewer for raising this issue. We have revised Figure 2D to a square (1:1) aspect ratio, as suggested, to improve readability. The updated figure is now included in the revised manuscript.

(11) Lines 681-682: when the definition of compensatory ability is the sum of incoming weights - although mathematically easiest, I am not sure what the sum represents. Because these weights are products, wouldn't a product be more natural? Not sure about this myself.

We thank the reviewer for raising this important issue. The graph direction to represent transitions from the existing background state to added substitutions. Each edge records the fraction of pairs showing a fitness increase ≥ 0.5. A product of incoming weights was not adopted because zero-valued weights would force the product to zero, obscuring differences in compensatory ability across substitutions.

Supplementary

(1) Figure S8 - the figure itself is confusing; I cannot connect it with the conclusion.

We apologize for the confusion caused by Figure S8. To address this, we have revised the figure layout and significantly expanded the legend to explicitly describe: (1) the origin and processing of the data, (2) the definition of the row/column of the heatmap, and (3) a direct interpretation to the corresponding conclusion. We believe the updated version now clearly conveys the intended message. The revised figure and legend are included in the updated supplementary materials.

(2) The font is inconsistent with the rest of the document.

We thank the reviewer for this careful observation. We have revised the font in the indicated section to match the formatting used throughout the manuscript. We have also reviewed the rest of the document to ensure overall formatting consistency.

We appreciate Reviewer #1’s careful comments on the rigor of the evolutionary framing and on the presentation of the manuscript. The revisions replace the landscape-altering language with statements about local neighborhoods, correct the inconsistent proportion reported in the Abstract, revise the two section titles so that they no longer restate a definitional property, number all equations, and improve the readability of Figures 1A, 1C, 2D, and S8.

Reviewer #2 (Public review):

Summary:

This manuscript presents an interesting and conceptually valuable analysis of compensatory evolution using a large combinatorial deep-mutational-scanning dataset for yeast His3p.

I particularly like the identification of "super compensatory" substitutions that improve fitness across diverse genetic backgrounds and apparently reduce the sensitivity of the local fitness landscape to subsequent mutations. The work connects epistasis, protein stability, mutational robustness, and evolvability in a clear and potentially broadly relevant manner.

The authors provide several complementary lines of evidence in support of this central conclusion. In particular, the new experimental validation of S189A is an important strength because it directly demonstrates that a predicted super compensator can buffer the effects of diverse deleterious substitutions, while analyses of additional DMS datasets from other proteins and assay systems suggest that the phenomenon is not restricted to the original His3p landscape.

We first appreciate Reviewer #2’s positive assessment of the conceptual value of the study, and in particular the recognition that the work connects epistasis, protein stability, mutational robustness, and evolvability, and that the new experimental validation of S189A is an important strength. We are also grateful for the three specific and constructive suggestions on structure-aware modelling, on the scope of the ProteinGym analysis, and on tree-aware testing of ortholog co-occurrence. These suggestions led to the largest additions in this revision. We have carefully considered each point, and our responses and the corresponding revisions are detailed below.

Weaknesses:

(1) The structural analysis currently relies primarily on correlations with RSA, weighted contact number, conservation, and Rosetta-predicted changes in folding or binding energy. For super compensators, the mechanistic evidence is largely limited to predicted stabilization and individual examples, such as the proposed salt bridge between 110D and R112. I believe that the newly developed structure-aware deep-learning approaches could provide useful information on the mechanism of super compensators. For example, an inverse-folding model such as ESM-IF1 could score complete multi-mutant sequences conditioned on the His3p backbone and test whether adding a super compensator restores sequence-structure compatibility across backgrounds. More recent multimodal mutation-effect or stability models could similarly be used to cross-check the Rosetta results, including models that explicitly support combinatorial mutations. I would not recommend simply comparing AlphaFold confidence scores between mutants, because current structure predictors are not necessarily sensitive to subtle mutation-induced energetic or conformational changes.

Following the reviewer's suggestion, we scored complete multi-mutant His3p sequences with ESM-IF1 (esm_if1_gvp4_t16_142M_UR50) conditioned on the 6EZM backbone, comparing exact measured genotype pairs that differ only by the state of interest (up to 1,000 backgrounds per state; 7,000 pairs). Five of the seven reported super compensatory substitutions in the Table S1 increased sequence–backbone compatibility: 144N (+0.0160), 169R (+0.0115), 110D (+0.0086), 189A (+0.0021) and 93V (+0.0016), each with a bootstrap interval excluding zero. Two decreased (73A, −0.0153; 137G, −0.0080). Against score-blind matched controls the contrast favoured the reported state for those same five (exact two-sided binomial P = 0.45). All seven directions were preserved in a contacting-chain context (chains A, R and L; Cα within 8 Å). We also used these scores to cross-check the archived Rosetta energies over the 1,217 exact pairs carrying archived entries on both sides (Zenodo 17769278). Higher archived energy accompanies lower measured fitness, so concordance would appear as a negative correlation; the observed Spearman correlations are positive (ρ = +0.085 to +0.094 pooled, +0.200 to +0.211 within focal state). The two predictors therefore do not track one another. We did not compare AlphaFold confidence scores between mutants.

In a word, ESM-IF1 supports the idea that most supercompensatory substitutions can promote the folding of His3p.

(2) The manuscript states that the pipeline was applied to 217 ProteinGym datasets and concludes that super compensators are broadly distributed across proteins and assays. However, this central generalization is described in only a few sentences and is largely relegated to Figure S7. The Methods do not explain which datasets contained sufficient combinatorial mutants to calculate compensatory ability or buffering, how many genotype pairs or quadruplets were available per substitution, or how differences in assay scale and library design were handled. This point requires clarification because super compensation is inherently a background-dependent property and cannot be established from single-mutant measurements alone. ProteinGym is widely used as a substitution-effect benchmark, and many of its constituent assays primarily contain single substitutions; for example, an analysis of an earlier ProteinGym collection reported that 76 of 87 assays contained only single substitutions. It is therefore unclear how the same compensatory-interaction pipeline could be applied uniformly to all 217 datasets.

We thank the reviewer for the suggestions. We have re-performed this analysis based on the pinned PG_v1.3 manifest. The 217 DMS assays cover 186 unique proteins. To identify super-competitors, we filtered for DMS datasets containing multiple substitutions per genotype—specifically requiring at least 10 sets of quadruplet genotypes to evaluate whether a specific amino acid state can mitigate mutational effects. This strict filtering yielded four qualified DMS datasets: three assayed for in vitro protein folding stability using cDNA display proteolysis (E3 ubiquitin-protein ligase AMFR, iron-regulated surface determinant protein H, and E3 SUMO-protein ligase CBX4; Tsuboyama et al., 2023), and one assayed for fluorescence intensity via FACS (green fluorescent protein 2; Gonzalez Somermeyer et al., 2022). We have updated the Methods section to detail this selection process.

(3) The analysis of 335 His3p orthologs in Discussion is potentially very interesting, but co-occurrence between super compensators and putatively deleterious amino-acid states does not by itself demonstrate evolutionary compensation. Closely related species share substitutions through common ancestry, and both states could be associated with a particular lineage or ecological context. A tree-aware analysis would considerably strengthen this result. The authors could reconstruct ancestral states and ask whether acquisition of a super compensator tends to precede or accompany otherwise deleterious substitutions. Alternatively, they could use phylogenetically informed permutations that preserve substitution frequencies and shared ancestry.

We agree. Co-occurrence among living species is not by itself evidence of compensation, because related species inherit substitutions from a common ancestor. We have therefore redone the analysis on a phylogeny, using the phylogenetically informed permutation the reviewer suggests.

We realigned the archived orthologs with MAFFT L-INS-i and built a maximum-likelihood tree with IQ-TREE: 329 species, 225 alignment columns, the Q. YEAST model selected by BIC, with 1,000 ultrafast-bootstrap and 1,000 SH-aLRT replicates. Six rows carrying three ambiguous duplicate species labels were removed, which also corrects the earlier figure caption that stated 355 species. We then tested 28 substitution pairs against a null in which both substitutions are simulated on the tree and thresholded to their observed frequencies, so the null preserves both how common each substitution is and how the species are related.

Two pairs stand out, and both involve 189A. 189A occurs together with 204I in 112 species, where the tree-based null expects 78 — an excess of 34 species. 189A occurs with 211E in 66 species against an expectation of 43 — an excess of 23. Both excesses are significant on their own under the tree-based simulation (p = 0.021 and 0.036, from 100,000 simulations) and under a separate Pagel test of correlated evolution (p = 0.046 and 0.023). No other pair reaches significance under both tests. 189A is also the substitution we validated experimentally, so the strongest evolutionary signal and the experimental result point to the same substitution.

We note two limits. Neither pair survives correction for having tested 28 pairs. And both pairs involve common substitutions (189A is present in 177 of the 329 species), so part of their high rank may reflect the greater statistical power available for common substitutions. We therefore present these as the strongest associations in the data rather than as proof of historical compensation.

We sincerely thank Reviewer #2 for recommending a broader mechanistic and evolutionary evaluation. The added ESM-IF1 analysis, the re-performed ProteinGym dataset selection, and the tree-aware analysis of ortholog co-occurrence provide more direct evidence for the properties of super compensatory substitutions, and we have stated the remaining limitations of each analysis explicitly.

Reviewer #3 (Public review):

The manuscript by Jiang and co-authors presents an analysis of experimental measurements (about 400k variants) from a deep mutational scan of the HIS3 enzyme. The authors assess the ability of a genotype to be "rescued" and show that this depends on mutation sites (in particular their solvent accessibility) and mutation effects (should be mild on folding stability or binding affinity). They further identify a set of super-compensatory mutations, and their results suggest that these mutations flatten the fitness landscape.

This finding is interesting and likely of interest to a broad community. The analysis seems sound. However, I have a number of major concerns regarding the presentation and positioning of the work.

We sincerely thank Reviewer #3 for the careful reading of our manuscript and for the positive comments that the finding is “interesting and likely of interest to a broad community” and that the analysis “seems sound.” The concerns regarding the positioning of the work relative to Pokusaeva et al. (2019), the description of the model used to estimate fitness potentials, the structural and citation details, and the sensitivity of rescuability to the threshold choices were valuable in improving the clarity and the rigor of the manuscript. We address each point below.

(1) It would improve the manuscript to clarify the present contribution with respect to a previous study by the same authors, namely Pokusaeva et al. 2019. Did the authors apply the same protocol to generate a new library of mutants, or did they re-analyse an already published library? If the library is not new, ambiguous sentences like "Nevertheless, to our knowledge, the His3p library remains one of the largest and most comprehensive resources that contains multi-site mutants" should be reformulated.

We thank the reviewer for noting this ambiguity; we agree and will revise accordingly. The large-scale His3p landscape was reported in Pokusaeva et al. (2019), and no new version was constructed here. Instead, we provide a computational re-analysis of those measurements to quantify rescuability, broad positive effects of super compensatory substitutions, and local buffering of fitness effects, plus a newly generated targeted DMS validation library (randomizing positions 181 and 202 in WT S189 vs. 189A) that experimentally validates compensation. To clarify provenance, we will change the sentence “Nevertheless, to our knowledge, the His3p library remains one of the largest...” to “While the large-scale library was measured previously (Pokusaeva et al., 2019), the current work combines a newly generated targeted dataset with a fresh re-analysis of this public His3p library to reveal previously unappreciated rules of compensation.” This revision clearly separates prior data from our novel contributions.

(2) Pokusaeva et al. 2019 is cited for the library and also for the deep neural network. It would be beneficial to briefly describe the architecture, the inputs and outputs, and the training procedure. Was the network trained on the current library? What is the purpose of this network? It looks more like an additive linear model (except for the global sigmoid) than a deep neural network. How does it relate to global epistasis models? The sigmoid function is designed to capture plateauing effects; doesn't that introduce some circularity issue in the reasoning?

Pokusaeva et al. (2019) describes a three-layer feed-forward model that is best understood as a global-epistasis model rather than a conventional deep neural network. The input is a one-hot encoding of amino-acid states. These inputs are first mapped to a one-dimensional additive latent variable, in which the state-specific coefficients are summed to produce a genotype-level latent “fitness potential.” That latent value is then passed through a learned nonlinear output layer with 22 units to generate the predicted fitness. The model was trained on the current library.

Its purpose is to separate the intrinsic contribution of each amino-acid state from the background-dependent saturation of the His3p assay. Raw fitness values are not directly comparable across genetic backgrounds: in already low-fitness backgrounds, additional substitutions may remain phenotypically invisible, whereas in high-fitness backgrounds, mildly deleterious effects may be masked. A global-epistasis formulation addresses this by placing states on an additive latent scale and capturing assay saturation through a monotonic nonlinear link function. In this framework, each state has an estimated coefficient that is interpreted as its background-independent fitness contribution.

This coefficient is not hypothetical; it is explicitly provided in File/DeepLearningWeights/DLWeightsFI.tsv as FI_mean, one row per state. These coefficients are used downstream to quantify each state’s fitness impact, which is essential for showing that supercompensatory substitutions are not defined in a circular way by construction.

(3) Are the super-compensatory mutations observed (conserved) across evolution? Beyond the fact that they are accompanied by mildly deleterious mutations in natural sequences. Can we predict them with variant effect predictors?

We thank the reviewer for these questions. Regarding evolutionary conservation, we have not performed a systematic phylogenetic analysis, as our primary focus here was the experimental characterization of compensation within the His3p system. Nevertheless, our data show that super‑compensatory mutations are consistently stabilizing across backgrounds (Fig. 4L)—precisely the property that makes them robustly beneficial regardless of context. This suggests that these mutations may be identifiable through stability‑predicting tools (e.g., FoldX, DeepDDG), which would flag them as stabilizing. Whether this stabilization is reflected in evolutionary conservation patterns is a separate question; while we observe their co‑occurrence with mildly deleterious variants in natural sequences (as the reviewer notes), we have not systematically tested whether conservation‑based predictors (e.g., EVE, DeepSequence) can predict them.

(4) The AAindex mention should be accompanied by a citation.

We thank the reviewer for the reminder. We will add the appropriate citation for the AAindex database in the revised manuscript

(5) Equations should be numbered. WCN formula seems to contain misformatting issues.

We thank the reviewer for the reminder. We numbered all equations sequentially and correct the formatting errors in the WCN formula.

(6) A more explicit description of the structural data analysed (which PDB entry?) should be provided.

We thank the reviewer for the reminder. The PDB entry used is 6EZM.

(7) I believe the citation Van Cleve and Weissman 2015 for the ProteinGym benchmark is incorrect. Additionally, is the Rosetta citation adequate?

We thank the reviewer for pointing out these citation issues. We have double-checked the references and agree with these concerns.

Regarding the Rosetta citation, we acknowledge that there is no single “Rosetta citation”. In our work, we used the ddg_monomer function for ΔΔG_fold calculations and the flex ddG function for ΔΔG of interface binding calculations. Therefore, we cited the corresponding methodological papers: Kellogg et al. (2011) for ddg_monomer and Barlow et al. (2018) for flex ddG.

(8) How is the definition of rescueability sensitive to the threshold choice?

We thank the reviewer for raising this important issue. To systematically evaluate the robustness of our rescuability measurements, we tested three key parameters: (i) the fitness cutoff used to define unfit genotypes, (ii) the minimum number of genotypes in the superset required for an unfit genotype to be considered and (iii) the fitness cutoff used to define fit genotypes. The first two parameters collectively determine the size of the unfit genotype set, while the third controls how rescuability was calculation.

As shown in Fig. S1D of the manuscript, varying the fitness cutoffs for defining both unfit and fit genotypes has only a minor effect on the calculated rescuability, as reflected by the highly correlated rescuability values across different cutoff combinations.

Besides, the primary goal was to examine how rescuability correlates with three biochemical features of each position in His3p: relative solvent accessibility (RSA), weighted contact number (WCN), and evolutionary conservation. When we applied different fitness cutoffs to define unfit genotypes while with at least 10 genotype in the superset, the correlations between rescuability and these biochemical features remained highly consistent (see Author response image 1A-D). This demonstrates that the observed associations between rescuability and RSA, WCN, and conservation are robust to the choice of fitness cutoff used to filter the unfit genotype sets.

We next assessed the sensitivity of our results to the superset (the whole genotypes with additional substitutions) threshold. Using a fixed fitness cutoff of zero to classify unfit genotypes, we found that, although this shifted the fraction of genotypes classified as unfit, the observed correlations between rescuability and the three biochemical features were largely unchanged, even when the superset was defined by as few as a single genotype (see Author response image 1E-F).

In summary, despite variations in the parameter settings used to filter unfit genotypes for rescuability calculation, the overarching conclusion—that rescuability is consistently correlated with RSA, WCN, and conservation—remains robust and reproducible across all tested conditions.

Author response image 1.

Different rescuability calculation methods and filtering thresholds produce similar results. (A-F) Different filtering thresholds used to calculate the average rescuability for each position of the monomer of His3p give similar results. (A-B) The average rescuability for each position along His3p for unfit genotype with fitness < 0.5. The total count of genotypes containing additional substitutions is at least 10. (C-D) The average rescuability for each position along His3p for unfit genotype with fitness < 1. The total count of genotypes containing additional substitutions is at least 10. (E-F) The average rescuability for each position along His3p for unfit genotype with fitness = 0 and the total count of genotypes containing additional substitutions is at least 1.

We are grateful to Reviewer #3 for the questions on data provenance, model description, structural data, citations, and threshold sensitivity. The revisions separate the previously published library from the newly generated targeted dataset, describe the global-epistasis model and its role explicitly, correct the citations, and document the robustness of rescuability across all tested filtering thresholds.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

While the results show some loss in the eyelid meibomian glands, there is significant gland retention in HSD3b6 KO mice, as shown in Figure 2. This is supported by the lack of DEG patterns showing downregulation of Meibum lipid genes (AWAT2, Far2, Soat1, Plin2, SCD, etc.), and no decrease in Pparg expression, known to be critical for meibomian gland lipid gene expression.

Weaknesses:

It should be noted that while the authors indicate that CD38 is significantly up-regulated in the HSD3b6 KO mouse, the increase was not sufficient to show a significant adjusted P-value. Bulk RNA sequencing also shows no significant change in meibum lipid gene expression for aged mice that are treated with 78c, an inhibitor of CD38, which the authors indicate increases NAD levels, leading to increased meibomian gland size compared to vehicle-treated mice.

Unfortunately, there was no increase in meibum lipid gene expression with 78c, as identified by adjusted P-value. However, it should be noted that the supplemental file covering DEG expression was labeled as a Microarray analysis. This did not include the 78c+NMN treated mice, which the authors contend show a more impactful effect on the meibomian gland.

We thank the reviewer for the careful evaluation of our work and for the constructive comments regarding the interpretation of the transcriptomic data and the molecular basis of meibomian gland dysfunction.

First, regarding the statistical significance of Cd38 expression in the microarray analysis, we performed additional validation using gene-specific quantitative PCR in independent eyelid tarsal plate samples. These new data are now presented in Fig. 2C, and the Results section has been revised as follows:

“… To validate the upregulation of Cd38, we performed real-time PCR analysis using gene-specific primers in independent eyelid tarsal plate samples, which confirmed a significant increase in Cd38 expression in Hsd3b6^−/− mice compared to Hsd3b6^+/+ controls. This difference was also observed in castrated mice; thus, the effect of Hsd3b6 deletion on Cd38 expression is independent of testicular testosterone (Fig. 2C).”

Second, we apologize for the error in the original supplementary DEG file, which caused confusion during the review process. We have now replaced it with a complete RNA-seq dataset that includes all expression values for aged mice treated with 78c+NMN (please see Supplementary Data 2). As shown in Fig. 4E, F, treatment with 78c+NMN significantly increased the expression of Elovl4 and Elovl7, elongases responsible for the synthesis of very long-chain fatty acids in the meibomian gland. We also re-examined representative meibum lipid-related genes (Awat2, Far2, Soat1, Plin2, and Scd1). Although none reached statistical significance individually, collective analysis of these representative lipid-related genes by two-way ANOVA with Bonferroni's post hoc test demonstrated a significant overall increase following 78c+NMN treatment in aged mice, compared with controls, supporting coordinated upregulation of the meibomian gland lipid synthesis program.

These analyses indicate that, although the individual lipid-related genes showed only modest changes, they exhibit a coordinated increase following 78c+NMN treatment in aged mice. By contrast, the same gene set showed no significant overall change in young (3-month-old) mice, consistent with the original RNA-seq results presented in Fig. 4E. To better illustrate these findings, we have summarized the expression of these representative genes in a new Supplementary Fig. S5 and revised the Results accordingly, as follows:

“…Furthermore, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited a coordinated increase following 78c-NMN treatment (Fig. S5). While the changes in individual genes were modest and did not reach statistical significance (Fig. 4E), analysis of the gene set as a whole demonstrated a significant overall increase compared with vehicle-treated controls.”

“In contrast, the same treatment in young mice did not significantly alter gene expression profiles (Fig. 4E, young), and no coordinated increase was observed for Awat2, Far2, Soat1, Plin2, or Scd1 (Fig. S5). This result is consistent with previous studies [44,47,48] showing that 78c (or NMN) exerts minimal effects in young mice compared with aged mice across multiple physiological parameters, including glucose homeostasis, exercise tolerance, and cardiac function.”

We also would like to note that the complete RNA-seq datasets provided in Supplementary Data 2 allow readers to examine the expression profiles of additional genes of interest.

Finally, regarding the observation that meibomian glands remain partially preserved despite the presence of gland atrophy in Hsd3b6^−/− mice, together with the limited significant changes in classical lipid-related genes, we agree that this is an important point for interpreting the mechanism(s) of meibomian gland dysfunction. Our previous transcriptomic analysis of FACS-purified meibomian acinar cells in Hsd3b6^−/− mice (PMID: 37117756) demonstrated reduced expression of genes involved in cell proliferation/differentiation, despite relatively preserved expression of canonical Pparg-dependent lipid genes. Our findings therefore extend the current framework by suggesting that meibomian gland atrophy can occur, at least in part, independently of detectable changes in Pparg expression, supporting the idea that intracrine steroidogenesis contributes to maintaining the proliferative activity of basal acinar cells alongside the Pparg-dependent pathway. Accordingly, we have revised the Discussion to clarify the relationship between our findings and the established Pparg-centred model of meibomian gland maintenance, as follows:

“Although 78c+NMN treatment effectively restored meibomian gland size, the molecular mechanisms underlying this recovery remain incompletely understood. Treatment with 78c+NMN significantly increased the expression of Elovl4, Elovl7, and Hsd3b6. However, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited only a modest coordinated increase following treatment. Interestingly, the expression of Pparg, a key transcriptional regulator of meibocyte differentiation and lipid synthesis [88-90], remained unchanged. These findings suggest that restoration of meibomian gland size by 78c+NMN does not require detectable changes in Pparg mRNA expression, although Pparg activity may instead be regulated at the level of protein abundance, subcellular localization, and/or post-translational modifications such as phosphorylation or SUMOylation [88,91].

Our previous transcriptomic analysis of FACS-purified meibomian gland basal acinar cells (meibomian precursor cells expressing androgen receptors) from Hsd3b6^−/− mice demonstrated impaired expression of genes involved in cell proliferation and differentiation despite relatively preserved expression of lipid-related genes [6]. In contrast, a recent single-cell study showed that Pparg expression progressively increases during meibocyte differentiation, although it is already detectable in basal acinar cells [92]. These observations suggest that Hsd3b6-dependent intracrine activity primarily supports the maintenance and proliferation of basal acinar cells, whereas the canonical Pparg pathway predominantly regulates subsequent meibocyte differentiation and lipid synthesis. Together, these findings suggest that Hsd3b6 dependent intracrine activity contributes to meibomian gland homeostasis through mechanisms that complement the Pparg-associated pathway. Thus, our findings extend the current framework by indicating that meibomian gland homeostasis is maintained not only through canonical PPARγ-mediated regulation but also through intracrine steroidogenesis.

Newly added references:

(88) Jester, J.V., Potma, E., and Brown, D.J. (2016). PPARγ Regulates Mouse Meibocyte Differentiation and Lipid Synthesis. Ocul Surf 14, 484-494. 10.1016/j.jtos.2016.08.001.

(89) Kim, S.W., Xie, Y., Nguyen, P.Q., Bui, V.T., Huynh, K., Kang, J.S., Brown, D.J., and Jester, J.V. (2018). PPARγ regulates meibocyte differentiation and lipid synthesis of cultured human meibomian gland epithelial cells (hMGEC). Ocul Surf 16, 463-469. 10.1016/j.jtos.2018.07.004.

(90) Hwang, H.S., Parfitt, G.J., Brown, D.J., and Jester, J.V. (2017). Meibocyte differentiation and renewal: Insights into novel mechanisms of meibomian gland dysfunction (MGD). Exp Eye Res 163, 37-45. 10.1016/j.exer.2017.02.008.

(91) Ahmadian, M., Suh, J.M., Hah, N., Liddle, C., Atkins, A.R., Downes, M., and Evans, R.M. (2013). PPARγ signaling and metabolism: the good, the bad and the future. Nat Med 19, 557-566. 10.1038/nm.3159.

(92) Zhu, X., Xu, M., Portal, C., Lin, Y., Ferdinand, A., Peng, T., Morrisey, E.E., Dlugosz, A.A., Castellano, J.M., Lee, V., et al. (2025). Identification of Meibomian gland stem cell populations and mechanisms of aging. Nat Commun 16, 1663. 10.1038/s41467-02556907-6.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors demonstrate strong correlations between a pro-inflammatory state, the activity of an intracrine hormone (3 beta-hydroxysteroid dehydrogenase, 3B-HSD), and the NAD co-factor. Specifically, in a 3B-HSD knockout mouse, there was an upregulation in proinflammatory cytokines and increased CD38+ cells (CD38 is an enzyme that depletes NAD, a necessary cofactor for 3B-HSD activity). Conversely, induction of inflammation in the eyelids resulted in reductions in 3B-HSD activity. Supplementation with 5 alpha-dihydrotestosterone (DHT) or the NAD precursor NMN, and inhibition of CD38 activity (78c), corrected the pathologies observed in both the 3B-HSD knockout mouse and the pro-inflammatory model (LPS injection into eyelids).

Strengths:

The experiments were performed with good rigor, assessing the impact of inflammation and 3BHSD activity using multiple model systems. The endpoints represented a combination of transcriptional changes, protein quantification, enzymatic activity, and immunofluorescent microscopy. The authors use human tissue from both younger and older individuals to justify their hypotheses that increased CD38 + cells and reduced 3B-HSD quantity exist in older individuals. The data provide the foundation for assessing more global changes to the tear film and ocular surface.

Weaknesses:

The main weaknesses of the study include the following:

(1) An absence of information on meibomian gland health, tear film, and ocular surface.

(2) Too few human subjects to validate the hypotheses.

Conclusion:

Overall, this study demonstrates an important relationship that exists between intracrine signaling, inflammation, and cofactor signaling. It represents a novel approach in therapeutic design for patients with meibomian gland dysfunction.

We thank the reviewer for the careful evaluation of our work and for recognizing the novelty and potential therapeutic implications of the relationship among intracrine signaling, inflammation, and NAD metabolism in meibomian gland dysfunction. We also appreciate the reviewer’s constructive comments on the limitations of the present study and areas for improvement in the manuscript.

Regarding the lack of information on meibomian gland health, tear film, and ocular surface, we have added a limitations section to explicitly acknowledge that these functional outcomes were not directly assessed in the present study. As the reviewer kindly noted, we only focused on a key pathological hallmark of MGD, namely age-associated tissue atrophy, and based on this we explored the NAD/3β-HSD/inflammation-mediated mechanism. Thus, a limitation of the present study is the lack of assessment of the downstream consequences of MGD. This point is now explicitly discussed in the manuscript; please note that additional details are provided in our responses to Reviewer #2’s Recommendations for the authors.

Regarding the human data, we added two additional human eyelid samples, increasing the sample size of the older group from 2 to 4. Nevertheless, we agree that the sample size remains limited and have now explicitly acknowledged this limitation in Discussion as follows:

“A caveat of this study is that the number of human eyelid samples analyzed was limited. Larger human cohorts will be necessary to establish the translational relevance of the age-associated CD38 accumulation observed in human tissues.”

Taken together, we believe that these revisions have clarified the scope and limitations of our present study.

Reviewer #3 (Public review):

Summary:

The authors aimed to investigate whether disruption of intracrine steroid hormone metabolism contributes to meibomian gland dysfunction and proposed a "vicious cycle" of gland dysfunction and inflammation, using a global Had3b6 knockout mouse model. The work addresses an important aspect of MGD, but its impact may be limited unless the intracrine mechanism can be more clearly distinguished from systemic hormonal effects.

Strengths:

This study addressed an important question. The hormonal regulation of the meibomian gland has long been recognized. If clarified, the concept of local steroid metabolism influencing gland homeostasis could have implications for understanding disease mechanisms and identifying therapeutic targets.

Weaknesses:

The use of a global knockout makes it difficult to separate local intracrine effects from systemic hormonal changes, and key controls and hormone measurements are lacking. LPS-induced inflammation may not reflect the chronic nature of MGD.

We thank the reviewer for the thoughtful evaluation of our work and for highlighting the importance of distinguishing local intracrine mechanisms from systemic hormonal effects. In response, we performed several additional experiments and substantially revised the manuscript. Specifically, we measured plasma testosterone and aldosterone levels and found no significant differences between Hsd3b6^−/− and Hsd3b6^+/+ mice. In addition, we repeated key experiments in castrated mice and observed that the effects of Hsd3b6 deletion on tarsal plate Cd38 expression and meibomian NAD levels were preserved despite the absence of testicular testosterone. These new findings provide additional support for a local intracrine mechanism in the eyelid. We also revised the Introduction and Discussion to better explain the proposed intracrine–inflammation vicious cycle and clarified the rationale and limitations of the LPS-based inflammation model, including its inability to fully recapitulate the chronic low-grade inflammation characteristic of MGD. Further details are provided in our responses to Reviewer #3’s Recommendations for the authors. We hope that these additions and revisions have strengthened the manuscript and addressed the reviewer’s concerns.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Overall, the authors need to provide bulk RNA sequencing data for all treatment groups and provide some explanation of the measurements in individual mice for gland growth.

We thank the reviewer for this helpful comment. We have now replaced the original supplementary file with a complete RNA-seq dataset that includes all treatment groups (Supplementary Data 2). In addition, as described in our response to the Public Review comment above, we extensively revised our manuscript to provide explanation of gene expression profiles (particularly, representative meibum lipid-related genes) in the dataset.

Accordingly, we have expanded the Results and reconstructed the Discussion by incorporating two new discussion paragraphs. The relevant revisions are provided below for your perusal:

“… Furthermore, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited a coordinated increase following 78c-NMN treatment (Fig. S5). While the changes in individual genes were modest and did not reach statistical significance (Fig. 4E), analysis of the gene set as a whole demonstrated a significant overall increase compared with vehicle-treated controls.”

“In contrast, the same treatment in young mice did not significantly alter gene expression profiles (Fig. 4E, young), and no coordinated increase was observed for Awat2, Far2, Soat1, Plin2, or Scd1 (Fig. S5). This result is consistent with previous studies [44,47,48] showing that 78c (or NMN) exerts minimal effects in young mice compared with aged mice across multiple physiological parameters, including glucose homeostasis, exercise tolerance, and cardiac function.”

“Although 78c+NMN treatment effectively restored meibomian gland size, the molecular mechanisms underlying this recovery remain incompletely understood. Treatment with 78c+NMN significantly increased the expression of Elovl4, Elovl7, and Hsd3b6. However, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited only a modest coordinated increase following treatment. Interestingly, the expression of Pparg, a key transcriptional regulator of meibocyte differentiation and lipid synthesis [88-90], remained unchanged. These findings suggest that restoration of meibomian gland size by 78c+NMN does not require detectable changes in Pparg mRNA expression, although Pparg activity may instead be regulated at the level of protein abundance, subcellular localization, and/or post-translational modifications such as phosphorylation or SUMOylation [88,91].

Our previous transcriptomic analysis of FACS-purified meibomian gland basal acinar cells (meibomian precursor cells expressing androgen receptors) from Hsd3b6^−/− mice demonstrated impaired expression of genes involved in cell proliferation and differentiation despite relatively preserved expression of lipid-related genes [6]. In contrast, a recent single-cell study showed that Pparg expression progressively increases during meibocyte differentiation, although it is already detectable in basal acinar cells [92]. These observations suggest that Hsd3b6-dependent intracrine activity primarily supports the maintenance and proliferation of basal acinar cells, whereas the canonical Pparg pathway predominantly regulates subsequent meibocyte differentiation and lipid synthesis. Together, these findings suggest that Hsd3b6-dependent intracrine activity contributes to meibomian gland homeostasis through mechanisms that complement the Pparg-associated pathway. Thus, our findings extend the current framework by indicating that meibomian gland homeostasis is maintained not only through canonical PPARγ-mediated regulation but also through intracrine steroidogenesis.”

Reviewer #2 (Recommendations for the authors):

The main suggestion for the study is the correlation with meibomian gland function. While the study correlates changes with 3B-HSD activity, pro-inflammatory cytokines, and NAD cofactor levels, there is little support describing the pathological changes to the meibomian glands and the impact on the tear film and ocular surface. The changes in the lipid profiles, tear film stability, aqueous tear production, ocular surface staining properties, corneal epithelial transcriptional abnormalities, and leukocyte infiltration into the corneal stroma could all be assessed. While the authors have done a thorough job of demonstrating the correlation of the three major factors listed above, the correlation with meibomian gland function is not completely assessed in the study.

We thank the reviewer for this insightful comment. We agree that functional assessments such as tear film stability, ocular surface pathology, lipid composition, and other downstream manifestations of MGD would complement the mechanistic findings reported here and provide additional insight into their physiological consequences.

However, the primary objective of the present study was to define the molecular mechanism underlying MGD, specifically the pathological interaction between meibomian gland intracrine activity and inflammation, and the role of the CD38–NAD axis in this process. Accordingly, our experiments were designed to focus on mechanistic endpoints directly related to this hypothesis, including 3β-HSD activity, NAD availability, inflammatory gene expression, and CD38 accumulation. In addition, we assessed a key pathological hallmark of MGD, namely age-associated meibomian gland atrophy and its recovery following 78c/NMN treatment.

While direct evaluation of tear film and ocular surface parameters was beyond the scope of the present mechanistic study, we agree that such analyses represent important future directions. To acknowledge this, we have added the following statement to the Discussion:

“… Firstly, while this study focused on defining the molecular and structural mechanisms underlying meibomian gland dysfunction, functional outcomes such as tear film stability, ocular surface integrity, meibum lipid composition, and other clinically relevant manifestations of disease were not directly assessed. Given the well-established link between meibomian gland dysfunction and tear film instability [57-59], future studies incorporating these functional assessments will be important to determine how the molecular and structural changes identified here contribute to ocular surface pathology and disease progression.”

The description of the vicious cycle seemed a bit out of place in the introduction. This would have been most appropriate in the conclusion/discussion in the manuscript. The general nature of the description lacked focus on the eyelids and meibomian glands, and the narrative took time to get to the interactions that would be assessed in the study.

We thank the reviewer for this insightful suggestion. We agree that the original Introduction placed excessive emphasis on the general concept of vicious cycles and that the discussion of disease-wide examples diverted attention from the specific focus of the present study on the meibomian gland.

In response, we substantially shortened and refocused the Introduction. Specifically, we removed the broad descriptions of vicious cycles in neurodegenerative, metabolic, and cardiovascular diseases. The revised Introduction now introduces the concept of a vicious cycle only briefly and moves more directly to the biological context of meibomian gland dysfunction and local intracrine steroidogenesis.

At the same time, we agree that the broader implications of this concept are better suited for the Discussion. We therefore added a brief concluding paragraph to discuss how our findings may inform the understanding of age-associated vicious-cycle processes in other diseases and may also provide a framework for considering intracrine-related pathology beyond the meibomian gland. The corresponding text has been added to the Discussion, as follows.

“Finally, although the present study focused on the eyelid meibomian gland, the concept of an intracrine–inflammation vicious cycle may have broader relevance. Self-reinforcing pathological processes are implicated in several age-associated diseases, and altered intracrine activity has been described in multiple extra gonadal and cancerous tissues [5,7,8,93,94]. Our findings may therefore provide a useful framework for understanding how local hormone metabolism contributes to the initiation and maintenance of tissue-specific pathological cycles during ageing.”

Reviewer #3 (Recommendations for the authors):

(1) Introduction:

(a) The first paragraph of the introduction defines the term "vicious cycle," but its relevance to the current study is low. It is not until line 54 that the specific tissue of interest is introduced. It is suggested that the beginning of the introduction be shortened to emphasize information that is directly relevant to the study.

We thank the reviewer for this helpful suggestion. We agree that the original opening of the Introduction was too general and that the specific focus of the study on the meibomian gland should be introduced earlier.

In response, we substantially shortened the first part of the Introduction. Specifically, we removed the broad discussion of vicious cycles across multiple disease contexts and revised the opening so that the concept of a vicious cycle is introduced only briefly. The revised Introduction now moves directly to the relevance of local intracrine steroidogenesis in the eyelid meibomian gland, thereby better emphasizing the biological context and focus of the present study.

At the same time, we recognized that some of the broader implications of the study remain important. Therefore, we incorporated these points into the Discussion, where we briefly discuss the potential relevance of intracrine–inflammation vicious cycles to other age-associated diseases and intracrine-related pathologies beyond the meibomian gland, as follows:

“Finally, although the present study focused on the eyelid meibomian gland, the concept of an intracrine–inflammation vicious cycle may have broader relevance. Self-reinforcing pathological processes are implicated in several age-associated diseases, and altered intracrine activity has been described in multiple extragonadal and cancerous tissues [5,7,8,93,94]. Our findings may therefore provide a useful framework for understanding how local hormone metabolism contributes to the initiation and maintenance of tissue-specific pathological cycles during ageing.”

(b) In the introduction, the authors should also include common types of intracrine hormones, such as DHT.

We thank the reviewer again for this valuable suggestion. In response, we revised the Introduction to include representative examples of intracrine steroid hormones, including 5α-dihydrotestosterone (DHT) and estrogens, together with a brief description of their local production and action within peripheral tissues. We believe that this addition helps clarify the concept of intracrinology for readers less familiar with the field.

“Common examples of intracrine steroid hormones include 5α-dihydrotestosterone (DHT) produced in the skin, prostate, and eyelid meibomian glands, as well as estrogens synthesized within the breast and endometrium [3-8]. These locally produced hormones act within the tissue in which they are synthesized.”

(c) The hypothesis of a "vicious cycle" in MGD is not fully explained. Specifically, how intracrine steroids drive the meibomian gland into a vicious cycle is not described. The current information only discusses a possible association between steroid hormones and meibomian gland health.

According to this important suggestion, we performed additional experiments and rewrote our introduction. Please note that plasma testosterone levels were not impaired in Hsd3b6^−/− mice and their eyelid proinflammatory phenotypes (compared to wt mouse eyelid) remained preserved in castrated mice. These data are now provided, by performing additional experiments (please see our replies to your comments, below). Taking these observations into account, we have tempered our introduction.

(2) Results:

(a) One major concern is that sex hormones have long been recognized to be associated with the meibomian gland and have been extensively studied (see the TFOS guidelines). There have also been clinical trials using androgens to treat MGD. With the global knockout of Had3b6, systemic sex hormone levels could also be altered, which may result in MGD (estrogens are synthesized from androgens and would therefore also be affected).

This thoughtful concern is well received, as we were not attentive to describe systemic testosterone in Hsd3b6^+/+ and Hsd3b6^−/− mice in our original manuscript (for which we should apologize). The corresponding plasma testosterone data are now incorporated as Fig. S1A and presented below for your perusal.

Importantly, plasma testosterone levels in Hsd3b6^−/− mice were comparable with those in wt Hsd3b6^+/+ mice, consistent with the known compensatory role of the paralogous enzyme Hsd3b1 in the mouse testis [21], which was confirmed to be expressed in Hsd3b6^−/− mice (see new Fig. S1B). This type of compensation by paralogous steroidogenic enzymes has also been reported in other knockout model, such as Hsd17b3^−/− mice, in which circulating testosterone levels were preserved due to a compensatory role of Hsd17b12 in the testis (new refs [83,84]). Based on these results, we rewrote our Results and Discussion, as follows.

“plasma testosterone levels were indistinguishable between Hsd3b6^−/− and Hsd3b6^+/+ mice (Fig. S1A), consistent with the known compensatory role of the paralogous enzyme Hsd3b1 in the mouse testis [21], which was confirmed to be expressed in Hsd3b6^−/− mice (Fig. S1B). These results indicate that local steroidogenic activity in the eyelid exerts anti-inflammatory effects independent of circulating testosterone levels.”

“For the interpretation of our meibomian intracrine activity model, it is important to note that in Hsd3b6^−/− mice, plasma testosterone levels were maintained at the levels comparable with those in Hsd3b6^+/+ mice (Fig. S1A). This appears due to a redundant expression of Hsd3b1 in the testis [6], although in the meibomian gland, Hsd3b6 is the sole enzyme (Fig. S1B) and accordingly its deletion causes the complete abolition of meibomian 3β-HSD activity [6]. The resilience of plasma testosterone levels has also been reported in a knockout mouse model deficient in Hsd17b3, a member of 17-ketosteroid reductase enzyme family required for the formation of testosterone [83], likely due to a potential compensatory role of the paralogous enzyme Hsd17b12 in the testis [84]. The Hsd3b6^−/− vs. Hsd3b6^+/+ phenotypes in the tarsal plate Cd38 expression and meibomian NAD levels were preserved in castrated mice (Fig. 2C, F), which provide additional evidence to support that non-systemic local steroidogenic activity in the eyelid, rather than circulating testicular testosterone, underlies the phenotypes observed in Hsd3b6^−/− mice.”

Newly added references:

(83) Lawrence, B.M., O'Donnell, L., Gannon, A.L., Smith, S., Curley, M.K., Darbey, A., Mackay, R., O'Shaughnessy, P.J., Smith, L.B., and Rebourcet, D. (2024). Compensatory mechanisms that maintain androgen production in mice lacking key androgen biosynthetic enzymes. FASEB J 38, e70177. 10.1096/fj.202402093R.

(84) Rebourcet, D., Mackay, R., Darbey, A., Curley, M.K., Jørgensen, A., Frederiksen, H., Mitchell, R.T., O'Shaughnessy, P.J., Nef, S., and Smith, L.B. (2020). Ablation of the canonical testosterone production pathway via knockout of the steroidogenic enzyme HSD17B3, reveals a novel mechanism of testicular testosterone production. FASEB J 34, 1037310386. 10.1096/fj.202000361R.

- For context, please note that plasma testosterone levels showed substantial inter-individual variability in both genotypes. Such variability is a well-established physiological feature of male mice, reflecting episodic testosterone secretion. Indeed, classical studies showed that variation in testosterone levels within the same mouse sampled on different occasions is comparable to that observed between individual mice, and a recent longitudinal LC–MS/MS study confirmed 10- to 100-fold fluctuations within individual adult male mice (Bartke and Dalterio, 1975, PMID: 1216260; Kettering et al., 2026, PMID: 41880754). Thus, the variability observed in our dataset is consistent with the known physiological dynamics of circulating testosterone in male mice.

(b) To support the hypothesis of intracrine regulation in MGD, the following would be essential:

- a local or targeted knockout model, and

- a global knockout with appropriate controls, such as Had3b6+/+ mice combined with gonadectomy.

Otherwise, the current study reflects the role of general steroid hormones in the meibomian gland rather than an intracrine-specific mechanism.

We repeated our experiments using castrated Hsd3b6^−/− mice. As shown in new Fig. 2C, we observed a significant increase in Cd38 expression in the tarsal plate of Hsd3b6^−/− mice (n = 6, castrated) as compared to Hsd3b6^+/+ control mice (n = 4, castrated). In addition, in Fig. 2F, we observed a significant decrease in NAD levels in the meibomian gland of Hsd3b6^−/− mice (n = 3, castrated) as compared to Hsd3b6^+/+ control mice (n = 5, castrated). These results provide additional evidence to support that local steroidogenic activity in the eyelid, rather than circulating testicular testosterone, underlies the phenotypes observed in Hsd3b6^−/− mice. Based on these results and consideration, we have modified our manuscript as follows.

“… This difference was also observed in castrated mice; thus, the effect of Hsd3b6 deletion on Cd38 expression is independent of testicular testosterone (Fig. 2C).”

“… Note that regardless of castration, Hsd3b6 deletion reduced meibomian gland NAD levels.”

“…The Hsd3b6^−/− vs. Hsd3b6^+/+ phenotypes in the tarsal plate Cd38 expression and meibomian NAD levels were preserved in castrated mice (Fig. 2C, F), which provide additional evidence to support that non-systemic local steroidogenic activity in the eyelid, rather than circulating testicular testosterone, underlies the phenotypes observed in Hsd3b6^−/− mice.”

(c) With the knockout of Had3b6, other steroid hormones may also be altered systemically, such as increased synthesis of the mineralocorticoid aldosterone. These hormonal changes could cause systemic effects such as hypertension, with unknown consequences for the meibomian gland. Please provide data on systemic steroid hormone levels to better interpret the current findings.

We thank the reviewer for raising this important point. To address the possibility that systemic mineralocorticoid alterations contribute to the observed meibomian gland phenotypes, we measured plasma aldosterone levels in Hsd3b6^−/− and Hsd3b6^+/+ mice. These new data are now included as Fig. S6.

Importantly, plasma aldosterone levels were not significantly different between Hsd3b6^−/− and Hsd3b6^+/+ mice (Fig. S6). This finding is consistent with the known expression pattern of steroidogenic enzymes in the adrenal zona glomerulosa, where both Hsd3b1 and Hsd3b6 are redundantly expressed and contribute to aldosterone biosynthesis (refs. 85-87). Thus, similar to the compensatory role of Hsd3b1 in maintaining systemic testosterone production in the testis, the redundant expression of Hsd3b1 in aldosterone-producing cells likely preserves systemic aldosterone levels in Hsd3b6^−/− mice.

Based on these new data, we have added the plasma aldosterone measurements as Fig. S6 and revised the Discussion accordingly. These results further support our conclusion that the phenotypes observed in Hsd3b6^−/− mice are unlikely to be secondary to systemic endocrine alterations and instead reflect the loss of local steroidogenic activity within the eyelid.

“…Plasma aldosterone levels were likewise preserved in Hsd3b6^−/− mice (Fig. S6), consistent with the redundant expression of Hsd3b6 and Hsd3b1 in the adrenal gland zona glomerulosa cells [85-87].”

(d) What is the age of the mice that underwent microarray analysis? The Methods section only specifies "young" and "old" without providing the actual ages. Although the ages can be inferred from the figures, they should also be clearly stated in the Methods section.

We thank the reviewer for this comment. We have now clarified the age of the mice in the Methods section. All mice used for the microarray analysis were age-matched and were 9 weeks old at the time of tissue collection (please see page 35, lines 818-819).

(e) Line 148: CD11b+ cells in the eye are usually referred to as dendritic cells derived from monocytes that function as antigen-presenting cells (APCs), rather than as phagocytes.

(f) Line 149: How was it determined that the CD38+ cells are macrophages? CD38 can also be expressed by T cells, plasma cells, NK cells, and other immune cell types.

Heeding these important instructions and based on their co-labeling with the myeloid marker CD11b, we have rewritten our Results on the cell identity of CD38 cells, as follows.

“… We also found that the myeloid cell marker CD11b stained the same cells (Fig. S2), indicating an increased number of myeloid immune cells that express CD38 in the tarsal plate of Hsd3b6^−/− mice (Fig. 2E, vs. Hsd3b6^+/+).”

In addition, to clarify that multiple immune cell types can contribute to CD38 expression in the tarsal plate and ocular tissues, we have extensively revised our manuscript by adding a new paragraph to the Discussion as follows.

“Secondly, the cellular identity of the CD38-expressing cells observed in the tarsal plate warrants careful interpretation. In the present study, we observed co-localization of CD38 with the myeloid marker CD11b, indicating that these cells are of myeloid origin. However, CD11b⁺ cells in ocular tissues such as in conjunctiva are often described as monocyte-derived dendritic cells functioning as antigen-presenting cells, rather than as classical phagocytic macrophages [95,96]. Therefore, our data do not allow us to further resolve the specific myeloid subpopulation (e.g., macrophages, dendritic cells, or other subsets) responsible for CD38 expression. In addition, CD38 is known to be expressed across multiple immune cell types, including T cells, plasma cells, and NK cells [97-99], suggesting that non-myeloid immune cells may also contribute to the overall CD38 signal in the tarsal plate. While previous studies in other tissues, such as in adipose tissue and liver [39,40], have attributed age-associated CD38 upregulation primarily to macrophages, our findings highlight the need for more precise cell-type–resolved analyses in ocular tissues. Future studies using lineage-specific markers or single-cell approaches will be required to define the exact cellular sources of CD38 and their respective contributions to NAD metabolism and inflammation in the eyelid.” Added references:

(94) Khandelwal, P., Blanco-Mezquita, T., Emami, P., Lee, H.S., Reyes, N.J., Mathew, R., Huang, R., and Saban, D.R. (2013). Ocular mucosal CD11b+ and CD103+ mouse dendritic cells under normal conditions and in allergic immune responses. PLoS One 8, e64193. 10.1371/journal.pone.0064193.

(95) Ahadome, S.D., Mathew, R., Reyes, N.J., Mettu, P.S., Cousins, S.W., Calder, V.L., and Saban, D.R. (2016). Classical dendritic cells mediate fibrosis directly via the retinoic acid pathway in severe eye allergy. JCI Insight 1. 10.1172/jci.insight.87012.

(96) Malavasi, F., Deaglio, S., Funaro, A., Ferrero, E., Horenstein, A.L., Ortolan, E., Vaisitti, T., and Aydin, S. (2008). Evolution and function of the ADP ribosyl cyclase/CD38 gene family in physiology and pathology. Physiol Rev 88, 841-886. 10.1152/physrev.00035.2007.

(97) Katsuyama, E., Humbel, M., Suarez-Fueyo, A., Satyam, A., Yoshida, N., Kyttaris, V.C., Tsokos, M.G., and Tsokos, G.C. (2024). CD38 in SLE CD4 T cells promotes Ca2+ flux and suppresses interleukin-2 production by enhancing the expression of GM2 on the surface membrane. Nat Commun 15, 8304. 10.1038/s41467-024-52617-7.

(98) Peralta Ramos, J.M., Castellani, G., Kviatcovsky, D., Croese, T., Tsitsou-Kampeli, A., Burgaletto, C., Abellanas, M.A., Cahalon, L., Phoebeluc Colaiuta, S., Salame, T.M., et al. (2025). Targeting CD38 immunometabolic checkpoint improves metabolic fitness and cognition in a mouse model of Alzheimer's disease. Nat Commun 16, 3736. 10.1038/s41467-025-58494-y.

(g) LPS-induced inflammation is acute and severe and may not accurately model MGD, which is typically characterized by chronic, low-grade inflammation. It is suggested to use a more relevant model, such as benzalkonium chloride exposure or a desiccating stress chamber.

We thank the reviewer for this important suggestion. We agree that benzalkonium chloride exposure and desiccating stress are widely used and well-established models for ocular surface inflammation and dry eye [30-35], and we have also tested these approaches in our experimental system. However, while these treatments reproducibly induced inflammatory responses in the cornea, conjunctiva, and meibomian orifice, we did not observe detectable inflammatory changes within the tarsal plate (i.e., the internal eyelid tissue containing the meibomian glands). To our knowledge, induction of inflammation in the tarsal plate by these approaches has not been reported in the literature. As such, in our current study, we adopted subcutaneous LPS injection into the eyelid. However, as noted by the reviewer, this approach represents an acute and relatively strong inflammatory stimulus and does not fully recapitulate the chronic low-grade inflammation characteristic of MGD. Please note that, by describing both the rationale and limitations of this approach, we have improved our manuscript as follows:

“Eye-drop instillation of inflammatory stimuli such as those by lipopolysaccharide (LPS) or benzalkonium chloride has been shown to be effective to cause inflammation in the cornea and conjunctiva [30-35]. However, we found this approach ineffective to induce inflammation in the tarsal plate (inside the eyelid tissue). Therefore, we performed subcutaneous injection of LPS to the eyelids (see Methods).”

Methods [Page 30, lines 694-701] “LPS (Sigma) was reconstituted in saline and injected subcutaneously (5 µg/eyelid) 8 h before tissue collection for qRT-PCR analysis. LPS was administered every other day for a total of three or six doses before the measurement of meibomian NAD⁺ concentration or meibomian 3β-HSD enzymatic activity, respectively. Subcutaneous microinjection was performed using an insulin syringe (Becton Dickinson, 30G). This LPS-based approach represents an acute inflammatory stimulus and does not fully recapitulate the chronic low-grade inflammation characteristic of MGD — while it provides a practical means to induce inflammation in the tarsal plate.” Added references:

(30) Lin, Z., Liu, X., Zhou, T., Wang, Y., Bai, L., He, H., and Liu, Z. (2011). A mouse dry eye model induced by topical administration of benzalkonium chloride. Mol Vis 17, 257-264.

(31) Lin, Z., He, H., Zhou, T., Liu, X., Wang, Y., Wu, H., and Liu, Z. (2013). A mouse model of limbal stem cell deficiency induced by topical medication with the preservative benzalkonium chloride. Invest Ophthalmol Vis Sci 54, 6314-6325. 10.1167/iovs.12-10725.

(32) Wu, M., Downie, L.E., Hill, L.J., and Chinnery, H.R. (2023). Topical Decorin Reduces Corneal Inflammation and Imparts Neuroprotection in a Mouse Model of Benzalkonium Chloride-induced Corneal Neuropathy. Invest Ophthalmol Vis Sci 64, 20. 10.1167/iovs.64.2.20.

(33) Wu, C.Y., Wu, M., Huang, X., Gu, B.J., Maldonado-Codina, C., Morgan, P.B., Downie, L.E., and Chinnery, H.R. (2022). Topographical Distribution and Phenotype of Resident Meibomian Gland Orifice Immune Cells (MOICs) in Mice and the Effects of Topical Benzalkonium Chloride (BAK). Int J Mol Sci 23. 10.3390/ijms23179589.

(34) Simmons, K.T., Xiao, Y., Pflugfelder, S.C., and de Paiva, C.S. (2016). Inflammatory Response to Lipopolysaccharide on the Ocular Surface in a Murine Dry Eye Model. Invest Ophthalmol Vis Sci 57, 2443-2451. 10.1167/iovs.15-18396.

(35) Corrales, R.M., Villarreal, A., Farley, W., Stern, M.E., Li, D.Q., and Pflugfelder, S.C. (2007). Strain-related cytokine profiles on the murine ocular surface in response to desiccating stress. Cornea 26, 579-584. 10.1097/ICO.0b013e318033a729.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This is a very elegant and convincing study. Using systematic screening of actin tail formation in two bacterial strains and employing a panel of CRISPR-CAS ko cell lines, the authors identify a novel dynamin-related GTPase GVIN, which forms an oligomeric coat around an intracellular Burkholderia strain. The bacterial O-antigen LPS layer is required for the formation of the GVIN coat, which disturbs the polar localization of the bacterial actin-polymerizing BimA protein.

I am not an expert in infection studies, but the experiments appear to be of high quality, the figures are well prepared, and clean and statistically significant results are provided. I have no criticism of the presented approaches.

The identification of a novel GBP1-independent pathway targeting intracellular bacteria is not only of fundamental importance for the immunity field but also of high interest to researchers in other areas, for example, evolutionary or structural biologists.

We sincerely thank the reviewer for their generous appraisal of our work. We appreciate their encouraging feedback.

Reviewer #2 (Public review):

Summary:

The authors wanted to investigate how cells defend against intracellular pathogens, such as Shigella and Burkholderia species, that co-opt the host actin machinery to spread from cell-to-cell. Previous work has identified IFNg-inducible GTPase of the Guanylate Binding Protein (GBP) family in cytosolic defence against Gram-negative bacteria. By forming a coat around Shigella, human GBP1 suppresses actin-based motility by displacing IcsA, which is the actin-polymerising virulence factor present at bacterial poles. In addition, GBP1 recruits the cytosolic LPS-sensor, caspase-4, to the bacterial surface, which results in the removal of bacterial replicative niches via pyroptotic cell death. Here, they followed up their finding that GBP1 can reduce actin-based motility of Shigella in HeLa cells and, surprisingly, fails to do so during Burkholderia infection. In contrast, in T24 bladder epithelial cells, GBP1 is competent in blocking Burkholderia actin-tails. They therefore wanted to identify the GBP1-independent factor that blocks actin-based motility in IFNγ-treated cells that is absent in HeLa cells.

Major strengths and weaknesses of the methods and results:

The authors report a second IFNγ-dependent pathway involving the protein product of the gene GVIN1, which was previously thought to be a pseudogene. GVIN1 (GTPase, very large interferon inducible 1) is thus the first human member of this family of ~250 kDa putative GTPases to be demonstrated to be functional and have potential antimicrobial roles. The discovery that GVIN1 is indeed functional, forms coats on Burkholderia in an LPS O-antigen-dependent manner, and limits actin-dependent motility are the main strengths of this paper. The authors use CRISPR/Cas9-based knockouts in HeLa and T24 cells, and complement them to demonstrate that GBP1 and GVIN1 are both required to inhibit actin-based motility.

An appraisal of whether the authors achieved their aims and whether the results support their conclusions:

The authors achieved their main goals through well-planned experiments and unbiased screens. They succeeded in finding the factor that blocks actin-based motility independently of GBP1. This is driven by GVIN1, which coats bacteria and limits actin-tail formation by reducing the expression of BimA through currently unknown mechanisms. Further, they found that an O-antigen mutant can escape coating by GVIN1, indicating the requirement for these polysaccharides in GVIN1-dependent bacterial sensing. However, the authors have not investigated whether GVIN1, which has two GTPase domains, does indeed have GTPase activity and whether GVIN1 and GBP1 together completely block cell-to-cell spread by Burkholderia and thereby restrict bacterial numbers over the infection time course. They also do not show whether GBP1 and GVIN1 target the same bacterial cell or different populations of bacteria.

A discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:

This work uncovers the antimicrobial actions of a member of yet another family of IFNg-induced GTPases, which potentially acts against other intracellular pathogens. GVIN1 appears to operate independently and in parallel to GBP1, pointing to the breadth and complexity of the IFNγ-inducible GTPase families.

We thank the reviewer for their overall positive assessment of our work and their suggestions for additional studies. We addressed all the comments and in response we have added additional experimental data to the revised manuscript. However, while we agree that a detailed biochemical characterization of GVIN1 protein is warranted, we consider such experiments outside of the scope of the current work.

Reviewer #3 (Public review):

Summary:

Here, Guo et al. (2025) propose that the IFN-induced GTPase GVIN1 forms a coat on cytosolic Burkholderia thailandensis, blocking actin tail formation through a mechanism analogous to GBP1-mediated restriction of Shigella motility.

Their study was prompted by the intriguing observation that IFNγ priming and GBP1 coat formation fail to inhibit B. thailandensis actin-based motility in HeLa cells, yet IFNγ restricts the motility of Burkholderia in T24 cells. Further investigation revealed that IFNγ restricts B. thailandensis motility in T24 cells via both GBP1-dependent and -independent mechanisms, suggesting that HeLa cells lack a critical GBP1 co-factor required to inhibit actin tail formation.

To identify the GBP1-independent mechanism, the authors performed an siRNA screen of interferon-stimulated genes (ISGs) and identified GVIN1, a large IFN-induced GTPase, as essential for restricting B. thailandensis motility. To identify the GBP1-independent mechanism, perform a knockdown screen for ISGs and find that the loss of GVIN, a very large IFN-induced GTPase, results in higher actin tail-positive B. thailandensis in T24 cells. They further demonstrate that GVIN forms coats on the surface of B. thailandensis, which prevent the polar localization of BimA and thus actin tail formation. In summary, the data reveal two independent IFNγ-induced pathways that restrict bacterial motility: one GBP1-dependent and the other GVIN1-dependent, each relying on distinct host co-factors.

Global assessment:

This is a well-executed study that convincingly demonstrates how GVIN1 restricts the actin-based motility of B. thailandensis through the assembly of coatomers. The results are clearly described, the manuscript is easy to follow, and the data are overall compelling and well presented. I have only a few suggestions on how the manuscript could be further improved.

We thank the reviewer for a clear summary of our findings, and we appreciate the reviewer’s thoughtful suggestions on our manuscript, which we addressed in our revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

GVIN/VLIG was previously described in the mouse, mostly. Why was it considered a pseudogene in humans? Some more background should be provided.

Major genome annotation projects (Ensembl, GENCODE, and RefSeq) rely on automated pipelines that flag loci as pseudogenes when they contain features incompatible with a single canonical open reading frame. These pipelines score in-frame premature stop codons, frameshifting indels, or the absence of a full-length matching transcript or protein in reference databases. The human GVINP1 locus displays several such features when compared against a naive single-ORF model of the mouse Vlig1 mRNA, and on that basis GVINP1 was likely categorized as a pseudogene by all three consortia, an assignment that has propagated through UniProt, HGNC, GeneCards, and OMIM ever since (UniProt Q7Z2Y8; GeneCards GVINP1). Importantly, these pipelines are not designed to detect loci that are expressed from more than one ORF or that produce a full-length protein through non-canonical translation, and they do not incorporate mass-spectrometry peptide evidence, ribosome profiling, or interferon-inducible expression data. Therefore, these automated pipelines can draw incorrect conclusions, as is the case here. We have added to the Introduction to provide a bit more background, as requested.

Is GVIN restricting the proliferation of the Burkholderia strain in the tested human cell line(s)? Is it restricting the intra-host mobility of the bacteria?

GVIN1 limits intracellular bacterial replication, albeit only modestly (see new data in Fig. S5B). We found that although GBP1 and GVIN1 block actin tail formation through independent, non-overlapping mechanisms, control of intracellular B. thailandensis burden required both proteins: IFN-γ failed to restrict bacterial replication in either GBP1KO or GVIN1KO T24 cells, and the loss-of-restriction phenotypes were quantitatively similar between the two knockouts (Fig. S5B). Together, these data identify GBP1 and GVIN1 as the effectors of two cooperating IFN-γ–induced defense pathways that jointly control B. thailandensis.

P 10: Remarkably, GVIN1 coatomers formed only infrequently on the surface of the O-antigen-deficient delta wbpm B. thailandensis mutant (Figure 5F). This information is not included in Figure 5F (only the quantification in E) and could be added.

We have added representative images of the corresponding microscopy data for both WT and DwbpM in a new Figure S8B.

Reviewer #2 (Recommendations for the authors):

Major points:

(1) The finding of GVIN1 as a protein is important and deserves further characterisation. For instance, it would be useful to investigate the transcripts they find in RNAseq, start sites, length of transcript, etc. There are two GTPase domains in this protein, but is either of them active as a GTPase if key GTP-binding and/or hydrolysis residues are mutated?

We agree that biochemical and enzymatic characterization of the GVIN1 protein is an important future direction. Similarly, careful investigations of GVIN1 expression, ribosome profiling, etc. ought to be conducted. However, these represent substantial, self-contained lines of investigation, and we will address them in a dedicated follow-up studies.

(2) Throughout the paper, the authors have only investigated the proximal steps of actin-tail formation. They do not go on to measure the impact of bacterial targeting by GBP1 or GVIN1, specifically in terms of bacterial spread cell-to-cell and replication (e.g., CFU measurements over time) and the impact on pyroptosis. Does GBP1 and/or GVIN1 targeting reduce bacterial CFUs over time?

re: 1) bacterial burden (CFU data); 2) host cell death (pyroptosis), and 3) cell-to-cell spread: 1) Our revised manuscript now provides CFU data (Fig. S5B) that identifies a modest impact on bacterial burden by GVIN1 expression – please, see also our response to Reviewer #1. 2) We already provided data in our original submission (Fig. S2D) demonstrating that IFNγ priming of either T24 WT or GBP1^KO cells did not appear to change the degree of host cell death in infected cells, as measured by Lactate Dehydrogenase (LDH) release assays. Accordingly, no further studies into host cell death pathways seem warranted at this time. 3) B. thailandensis is unusual among cytosolic bacterial pathogens in that it can spread between host cells not only through actin tail–driven propulsion but also via flagellar motility (PMID: 21730143). Therefore actin-based motility is not essential for cell-to-cell spread for this specific organism (PMID: 21730143). Consistent with this dual-mode dissemination, IFN-γ priming of WT T24 cells had no measurable impact on plaque-based cell-to-cell spread (new data in Fig. S5A), despite sharply reduced actin tail formation inside IFN-γ primed WT T24.

(3) The enumeration of microscopy could be improved by providing the % of GBP1+ve or GVIN1+ve bacteria that are actin-ve.

We added those data presentations as new panels Fig. S2G for GBP1 and Fig. S7B. As expected, these data show that under IFN-γ primed conditions GBP1-coated or GVIN1-coated bacteria fail to form actin tails.

(4) The authors show a schematic of GBP1 and GVIN1 targeting the same bacterial cell, but they have not demonstrated this experimentally. For many of their claims, it is important to show GVIN1 and GBP1 co-staining during infection with WT and the wbpM mutant Burkholderia.

The schematic depicted GBP1 and GVIN1 on opposite sides of the same bacterium purely for illustrative clarity and was not intended to convey that GBP1 and GVIN1 necessarily coat the same bacterial cell. We agree, however, that whether GBP1 and GVIN1 coatomers can co-decorate a single bacterium is a mechanistically interesting question, and we have now addressed it experimentally. Dual immunostaining in IFNγ-primed cells showed that most targeted bacteria were encased by either a GBP1 or a GVIN1 coatomer, but not both (Fig. S7C). A small subpopulation of GBP1/GVIN1 double-positive bacteria was nonetheless detectable (Fig. S7C–D), indicating that the two coat types are largely, but not strictly, mutually exclusive. The rarity of dual-coated bacteria reinforces our conclusion that the two coatomers operate as predominantly independent effector systems, consistent with their ability to restrict actin tail formation independently of one another.

(5) The authors make points about GBP1 and GVIN1 as being independent pathways and the need for a cofactor. To be certain about these conclusions, have they co-expressed both GBP1 and GVIN1 together in double knockout HeLa & T24 and assessed outcomes? They started out to look for a GBP1 cofactor that is required in HeLa cells, but they found GVIN1, which seems to operate independently of GBP1 (which is not inherently an issue, but I feel this needs to be clarified better). In T24 cells, expression of (mCh-)GBP1 alone without IFNg priming does reduce Actin+ve bacteria (Figure 2C, green bars), so GBP1 can use a factor that is expressed in naïve cells? But the authors have not shown that this factor is GVIN1. The same is true for GVIN1 expressed without IFNγ in T24-GVIN1-/- (Fig 5C). What happens in a similar experiment with an O-antigen mutant?

We believe the individual experiments the reviewer proposes have, in fact, already been performed in some fashion and are presented in the manuscript. Because these experiments are distributed across several figures, we have taken this opportunity to summarize the logic here and to point the reviewer to the relevant panels.

First, we would like to clarify the origin of GVIN1 in our study, as the reviewer's framing suggests that we set out to identify a GBP1 co-factor and instead landed on GVIN1. Our siRNA screen (Fig. 4A–B) was in fact designed to identify ISGs required for the GBP1-independent anti-actin-tail pathway and was therefore conducted in a GBP1^KO T24 background. GVIN1 emerged as a factor whose depletion restored actin tail formation in the absence of GBP1, and it is therefore, by design of the screen, an effector of a GBP1-independent pathway rather than a candidate GBP1 co-factor.

Second, we show that single deletion of either GBP1 or GVIN1 produces a partial and quantitatively similar de-restriction phenotype, whereas only the DKO fully abolishes IFNγ-mediated restriction of actin tail formation (Fig. 4C). Thus, we are seeing the classical additive signature of two non-redundant pathways acting on the same phenotype. In the gain-of-function direction, ectopic re-expression of GVIN1 in the DKO background restores IFNγ-dependent restriction to a level indistinguishable from the GBP1^KO single knockout (Fig. 5D). A reciprocal experiment co-expressing both GBP1 and GVIN1 in the DKO would only test for additivity of two effects we have already shown to occur independently and would not provide an orthogonal test of independence beyond what Fig. 4C and Fig. 5D already establish.

Third, we do not think GVIN1 is a likely candidate for the basal GBP1 co-factor that the reviewer infers from Fig. 2C. GVIN1 is IFNγ-inducible and effectively absent from unprimed T24 cells (the putative co-factor, while IFNγ-inducible, would be expected to be expressed at appreciable levels in naïve cells). Indeed, GVIN1 entered our screen precisely because of that inducibility (Fig. 4A and RNA-seq data in Fig. S3A–B). More decisively, we show that IFNγ-primed HeLa cells allow for ectopically expressed GVIN1 but not for ectopically expressed GBP1 to restrict actin tail formation. In other words, the ISG co-factor for the GVIN1 pathway must be distinct from the ISG co-factor for the GBP1 pathway. Lastly, we now show that GBP1 and GVIN1 coatomers are largely mutually exclusive, further arguing against GVIN1 acting as the GBP1 co-factor or vice versa in blocking actin tail formation.

Fourth, the O-antigen mutant experiment the reviewer asked about has also been performed and provides another point of mechanistic separation between the two pathways. Ectopically expressed GVIN1 assembles a coatomer on WT B. thailandensis but only rarely on the ΔwbpM O-antigen-deficient mutant (Fig. 5F). This observation parallels (and thus mechanistically explains) why ΔwbpM is resistant specifically to the GBP1-independent (i.e., GVIN1-dependent) branch of IFNγ defense (Fig. 3E). GBP1, by contrast, engages both B. thailandensis WT and the O-antigen ΔwbpM mutant efficiently (new Fig. S8C).

Taken together, four convergent lines of evidence (additive genetics in the DKO (Fig. 4C), cross-complementation of GVIN1 in the GBP1-null background (Fig. 5D), non-overlapping co-factor requirements in HeLa versus T24 cells (Fig. 2, Fig. 5), and distinct O-antigen dependencies for the two coatomers (Fig. 5E, Fig. 8C)) establish that GBP1 and GVIN1 constitute two parallel, independently operating antimicrobial modules, each likely with its own set of IFN-inducible co-factors.

(6) The discussion does not currently discuss GBP1/Caspase-4-driven pyroptosis as a host-defence mechanism, which should be included. The authors should also discuss why Shigella and Burkholderia are differentially targeted, given the differences in the mechanism of actin polymerisation by IcsA and BimA.

We previously showed that a GBP1 polybasic motif mutant that is unable to form coatomers on bacteria remains able to activate Caspase-4-driven pyroptosis and thus demonstrated that coatomers are not strictly required for GBP1-dependent Caspase-4 activation (PMID: 37023136). We now provide this information in the Discussion of the revised manuscript.

We provide new data showing that GVIN1 forms coatomers on BimA-deficient and WT B. thailandensis with similar efficiency (new Fig. S8A) and we previously demonstrated that icsA plays no role in GBP1 coatomer formation (PMID: 33885766). Therefore, actin polymerization appears to play no role in either GVIN1 or GBP1 coatomer formation.

Minor points:

(1) Have the authors used anti-actin antibodies or phalloidin staining? Please clarify.

We used phalloidin staining and this information is now also provided in the Results section (lines 118-119) in addition to the Materials and Methods section of the paper.

(2) Provide the Gene ID, Ensembl ID, etc., for GVIN1 at first mention.

We inserted the text: “Because automated annotation pipelines flag predicted in-frame stop codons, GVIN1 has long been catalogued as the pseudogene GVINP1 (GTPase, Very large IFN-Inducible Pseudogene-1) by Ensembl, GENCODE, and RefSeq (HGNC 25813; NCBI Gene 387751; OMIM 616121).” in the Introduction (lines 104 – 107)

(3) The bond linking the core sugars with the O-antigen is missing in the schematic of LPS in Figure 3A. Please mention which sugars these are, if it is known for Burkholderia.

We have corrected the schematic (Fig.3A) to include the bond linking the core sugars with the O-antigen.

(4) RNA-seq datasets should be deposited to GEO or similar public databases, and project IDs provided.

The RNA-seq datasets was deposited to the NCBI Gene Expression Omnibus (GEO), and the project accession IDs are is cited in the Data Availability statement.

(5) The description of the transcriptomics analyses was not clear - are the heatmaps in Figure S3 of genes that were induced by IFNg in these cell lines, but not HeLa or A594, but the description states fold-change over naïve cells?

The reviewer is correct and we apologize for the error in the figure legends, which we edited to clarify that the heatmap compares gene expression across IFNγ-primed cell lines.

Reviewer #3 (Recommendations for the authors):

Major comments:

(1) It would be nice to include some additional analysis on GVIN: GBP1 and GVIN1 seem to recognize different structures and need different cofactors. Are they structurally similar (alignment)? Can you map functionally important GBP1 regions on GVIN1, such as a polybasic motif, similar to motifs found in GBP1? Or does GVIN have a lipidic membrane anchor or a CAAX box? In other words, is GVIN binding directly to the outer membrane or through the unknown cofactor? Is GVIN an effector of another protein that binds to the OM?

Detailed structural studies including the mapping and biochemical characterization of GVIN1's membrane-targeting domain(s) represent substantial, self-contained lines of investigation that are beyond the scope of this study and that we hope to present in a future follow-up study.

(2) In T24 cells, GVIN1 and GBP1 (and their cofactors) get induced upon IFNg priming. Upon B. thailandensis infection, is it possible to see mixed or double coats? Does GBP1 have a higher affinity for Shigella and GVIN for B. thailandensis? Is GVIN1 B. thailandensis-specific? It would be a nice addition to discuss other virulent Burkholderia species that make actin tails (such as B. pseudomallei) to further enhance the possible relevance of GVIN1.

Please see our response to reviewer #2: dual immunostaining in IFNγ-primed cells showed that most targeted bacteria were encased by either a GBP1 or a GVIN1 coatomer, but not both (Fig. S7C). A small subpopulation of GBP1/GVIN1 double-positive bacteria was nonetheless detectable (Fig. S7C–D), indicating that the two coat types are largely, but not strictly, mutually exclusive. Re: the measurement of GBP1/ GVIN1 affinities for different bacteria – we agree that this is an area of future exploration but not within the scope of this study. Extending research on GVIN1 to other bacterial organisms including other Burkholderia species is indeed among our future research goals. We more broadly speculate on the potential importance of GVIN1-mediated host defense targeting other Burkholderia species in the Discussion (see lines 363 ff)

(3) In panel F of Figure 6, It appears that GVIN forms full coats in the absence of IFNγ priming, but relocalizes to the bacterial poles upon IFNγ treatment. Is this shift in localization a representative and consistent observation, or could it be an artifact of the specific image selected? Additionally, could this relocalization be driven by the presence of IFNγ-induced cofactors? For example, might GVIN interact directly with BimA, or could an IFNγ-dependent cofactor mediate its recruitment to the poles?

We believe the author is commenting on Figure 5F instead of 6 based on the question. The perceived shift in GVIN1 localization to the bacterial pole under IFNγ-primed conditions was not something we routinely observe and the original image shown in Fig. 5F is likely an outlier. We therefore replaced the original image with a more representative image.

(4) The authors conclude that BimA is eliminated from the outer membrane, but it is unclear what evidence this conclusion is based on. Could it be that BimA is not eliminated, but rather becomes diffusely distributed in the membrane in the presence of GVIN1, and is therefore more difficult to detect by microscopy? One way to test this hypothesis would be to delete BimC. If BimA localization is indeed dependent on BimC, its signal should become diffuse. If a BimA signal can be detected in BimC-deficient bacteria, but not in GVIN-positive bacteria, it would indeed strengthen the claim that BimA is removed from the membrane.

Prior literature demonstrates that on a bimC mutant, BimA remains detectable on the bacterial surface in a dispersed manner and that this dispersed BimA localization correlates with an "actin cloud" surrounding the bacteria. In our GVIN1-coated bacteria, we do not detect an actin cloud or residually localized BimA signals. We have now mentioned this in the Results section line 305 - 308 referencing this published phenotype to strengthen our argument that BimA is likely cleared from the membrane rather than merely redistributed.

(5) The siRNA mini-screen would benefit from appropriate controls demonstrating that the targeted genes were effectively knocked down. Without this, it's difficult to interpret negative results with confidence. It remains possible that the co-factor of GVIN1 is among the ISGs tested, but that the knockdown was insufficient to produce a detectable phenotype.

We now acknowledge this limitation. We have updated the text on lines 221-223 to explicitly state that our mini-screen does not rule out potential false negatives due to varying knockdown efficiencies.

(6) The authors convincingly demonstrate that GVIN1 coats prevent actin tail formation by B. thailandensis, but they do not explore the broader biological consequences of this observation. An important next step would be to assess whether GVIN1 coating restricts B. thailandensis cell-to-cell spread. By 8 hours post-infection, a clear difference in spread should be observable if actin-based motility is impaired. Additionally, it would be valuable to determine whether GVIN1-coated bacteria are still capable of intracellular replication. These functional assays would provide important insight into the biological relevance of GVIN1-mediated coating.

We have now assessed the effect of GVIN1 on intracellular bacterial replication (see new CFU data in Fig. S5B) and cell-cell motility (see new data in Fig. S5A). Please, also refer to our comments in response to Reviewer 1 for more details.

(7) As far as I am aware, the exact function of the GBP1 coat remains unclear. The authors refer to their earlier work (Kutsch et al., 2020) and claim to have demonstrated an "emulsifying activity." However, this overinterpretes the findings of that publication, since Kutsch et al. (2020) showed that the GBP1 coat disrupts the barrier function of the O-antigen, rather than compromising the integrity of the outer membrane itself. This disruption increases bacterial susceptibility to polymyxin B, but does not show an 'emulsifying effect'. Furthermore, the same group later reported that GBP1 exhibits an "aggregating" activity on LPS micelles (Dickinson et al., 2023), which seems to contradict the notion of an emulsifying function. I would recommend tempering the current claims about GBP1's activity. The precise impact of the GBP1 coat on the bacterial outer membrane remains unresolved and should be presented as an open question.

Our previous work demonstrated GBP1 coatomers on the bacterial surface disrupt the membrane-stiffening and membrane-shielding activities of O-antigen. We stand by the interpretation of our results and think it is likely that GBP1 coatomers act like surface-active agents or emulsifiers. However, we agree with the reviewer that more biophysical studies are needed to definitively test this model. Accordingly, we have revised some of the language and clearly articulated that GBP1 coatomers acting as a surfactant is a model that we are proposing.

As the reviewer correctly stated we have also shown that GBP1 can aggregate “free” LPS, i.e. to act more like a flocculant. Substances that are both flocculants and surfactants exist (e.g. long-chain fatty acid soaps). However, these substances typically do not act as flocculants and surfactants simultaneously under the exact same conditions. Similarly, we propose that GBP1’s role depends on context: we propose that GBP1 coatomers on the bacterial surface act as surfactants, while polymerizing GBPs bound to LPS acts a flocculant.

Minor comments:

(1) Figure 3: Can a GBP1 coat assemble on the delta wbpM mutant of B. thailandensis? The authors suggest GBP binds to the O-antigen, but other publications suggest that the O-antigen is dispensable in certain bacteria.

We conducted these experiments – see also our response to reviewer #2. Briefly, ectopically expressed GVIN1 assembles a coatomer on WT B. thailandensis but only rarely on the ΔwbpM O-antigen-deficient mutant (Fig. 5F). GBP1, by contrast, engages both B. thailandensis WT and the O-antigen ΔwbpM mutant efficiently (new Fig. S8C). We do not argue that GBP1 requires O-antigen binding for coatomer formation on Burkholderia. However, direct or indirect interactions between GVIN1 and O-antigen may be required for GVIN1 coatomer formation.

(2) Figure 4: GBP6 appears as a hit in the T24 screening but turned out to be a false positive. How does that look in the other cell lines that were part of the screen (U937, THP1)?

the characterization of T24 GBP6^KO cells clearly demonstrated that GBP6 is dispensable for either the GBP1 or the GVIN1 pathway in these cells. While we cannot formally rule out that GBP6 would be required for the GBP1/GVIN1 pathways in other cell lines, there are no compelling arguments in favor of this model – as far as we can tell - and we therefore did not investigate this further.

(3) Figure 5F: Please show the blots confirming exogenous GVIN expression.

We have provided an immunoblot showing the expression of exogenous GVIN1in HEK293T cells in new Fig. S7A

(4) Figure 6: Can you induce GVIN expression after actin tails have been formed and stop disassembling them?

This is an interesting idea and will require a technically challenging video microscopy approach that we will consider for future investigations.

(5) Figure 6: Are the bacteria showing no BimA signal GVIN1-coated? Eventually, stain for LPS to see if bacteria are lacking BimA also lack LPS.

Our preliminary studies indeed support this and thus indicate that the elimination of BimA from the bacterial surface requires the concerted effort of the GVIN1 coatomer and its putative co-factor (or the GBP1 coatomer and its putative co-factor, respectively). A detailed characterization of the mechanism by which BimA is removed from the bacterial surface will be part of future studies.

Author response:

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

Public Reviews:

Reviewer #2 (Public review):

Summary:

This paper attempts to examine how rare, extreme events impact decision-making in rats. The paper used an extensive behavioural study with rats to evaluate how the probability and magnitude of outcomes impact preference. The paper, however, provides limited evidence for the conclusions because the design did not allow for the isolation of the rare, extreme events in choice. There are many confounding factors, including the outcome variance and presence of less-rare, and less-extreme outcome in the same conditions.

Strengths.

(1) The major strength of the paper is the significant volume of behavioural data with a reasonable sample size of 20 rats.

(2) The paper attempts to examine losses with rats (a notoriously tricky problem with non-human animals) by substituting time-outs as a proxy for losses. This allows for mixed gambles that have both gain and loss possible outcomes.

(3) The paper integrates both a behavioural and a modelling approach to get at the factors that drive decision-making.

(4) The paper takes seriously the question of what it means for an event to be rare, pushing to less frequent outcomes than usually used with non-human animals.

Weaknesses:

(1) The primary issue with this work is that the primary experimental manipulation fails to isolate the rare, extreme events in choice. As I understand the task, in all the conditions with a rare extreme event (e.g., 80 pellets with probability epsilon), there is also a less-rare, less-extreme event (e.g., 12 pellets with probability 5). In addition, the variance differs between the two conditions. So, any impact attributable to the rare, extreme event could be due to the less rare event or due difference in the variance (or other statistical moments, like skew or kurtosis). That the distributions can be shown to be different under specific assumption to value maximizing agents (e.g., with Jensen Gaps and Table 2) is not really relevant to what rats are sensitive and what drive their behaviour. The design here does not support the conclusions. Finally, by deliberately confounding rarity and extremity, the design does not allow for assessing the impact of either aspect on rat behaviour.

This is a repetition almost word for word of point (1) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(2) The RL modelling work also fails to show a specific impact of the rare extreme event. As best as I can understand Eq 2, the model provides a free parameter that adds a bonus to the value of either the two options with high-variance gains (A and V in the paper) or to the two options with high-variance losses (F and V in the paper). Or equivalently to the ones with "Jackpots" vs the ones with "Black Swans" (see Point 1 above as to how these different aspects are all confounded in this design). This parameter seems to only depends on whether this option could have possibly yielded the rare, extreme outcome (i.e., based on the generative probability) and was not connected to its actual appearance. [This point is unclear as the text says this, but the rebuttal states otherwise; plus some options never received the REE, see Table S11]. That makes it a free parameter that just bumps up (or down) the probability of selecting a pair of options. That may be due to presence of the REE or the other rare event or just the variance difference. Moreover, in the case of the "black swan" or high-variance loss conditions, this seems very much like a loss aversion parameter, but an additive one instead of a multiplicative one. Is there a theoretical claim here that "extreme losses" need an additive loss-aversion parameter?

This is a repetition almost word for word of point (2) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(3) The paper presented the methods and results with lots of neologisms and fairly obscure jargon (e.g., fragility, total REE sensitivity). That might it very hard to decipher exactly what was done and what was found. For example, on p. 4, the use of concave and convex was very hard to decipher; the text even has to repeat itself 3 times (i.e., "to repeat" and "in other words") and is still not clear. It would be much clearer (and probably accurate) to say that the options varied along the variance dimension, separately for gains and losses. Option A was low-variance gains and losses. Option B was low-variance losses and high-variance gains. Option C was high-variance losses and low-variance gains, and Option D was high-variance losses gains. That tells much more clearly what the animals experienced without the reader having to master a set of new terminologies around fragility and robustness, which brings a set of theoretical assumption unnecessarily into the description of the experimental design. Alternatively, if the authors are wary of using the term "variance" because other moments of the distribution also differ, they could use "high-value gains" or "high-value losses" or something else which does not obscure the experimental design with jargon. Again, this goes back to point 1 above, whereby the different options differ on so many dimensions (as is made even more apparent in the rebuttal) that the design cannot isolate the impact of the variables of interest.

This is a repetition almost word for word of point (3) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space. The new words that we use are an attempt at reflecting the novelty of the approach and design.

(4) Were the probabilities shuffled or truly random (seem to be fixed sequences, so neither)? What were the experienced probabilities? Given the fixed sequences, these experienced ("ex-post") probabilities, could differ tremendously from the scheduled ("ex ante") probabilities. It's quite possible than an animal never experienced the rare, extreme event for a specific option. From Table S11, that is guaranteed to have happened in that 4 animals only ever experienced the "black swan" outcome once. It's even possible (if they only picked a specific option on the 10th/60th choices by chance), that they only ever experienced that rare extreme event. This point still cannot be known given the information provided, which does not break down outcomes by options. The Supplemental in Table S11 only gives overall numbers but does not indicate what the rats experienced for each choice/option-which is what matters here. A simple table that indicates for each of the 4 options, how often they were selected, and how often the animals experienced each of the 6-8 possible outcome would make it much clearer how closely the experience matched the planned outcomes. In addition, by restricting the rare outcome to either the 10th or 60th activations in a session, these are not random. Did the animals learn this association? The text states that they did not, but no evidence is provided.

This is a repetition almost word for word of point (4) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(5) The choice data are generally presented in an over-processed fashion with a sum and a difference (in both figures and tables). The basic datum (probability/frequency of selecting each of the 4 options) is not provided directly in the main text, even if it can theoretically be inferred from the sum and the difference. New right side of Table S4 is probably the most valuable piece in terms of explaining what rats did and should be highlighted a lot more. Inspection of that table reveals some interesting (and potentially worrying) results. Most notably, the vast majority of responding happens on the "anti-fragile" and "robust" option, often totalling around 90% of all selections, especially amongst the most common blue rats. Alas, those were all those the two options that were deliberately assigned to the two most preferred holes in the training phase (see p. 26). Does this reflect genuine preference for reward distributions or does this reflect a spatial hole bias? The assignment strategy makes this impossible to tell apart.

This is a repetition almost word for word of point (5) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space. In addition, in Figure 8 of Material and Methods, we report the changes in behavior between the training and final sessions. The related discussion stresses that half of the rats changed more than 30% of their choices in the final experimental sessions compared to the training sessions. See also our previous reply to point (8).

(6) There is insufficient detail provided on the inferential statistical tests (e.g., no degrees of freedom or effect sizes), and only limited information on exactly what tests were run and how (bootstrapping, but little detail). Without code or data (only summary information is provided in the supplement), this is difficult to evaluate. In addition, the studies seem not to pre-registered in any way, leaving many research degrees of freedom. Not all studies need to be pre-registered and sometimes discovery of new things requires exploratory work, but preregistration does provide additional safeguards against overemphasizing post-hoc detected patterns-a serious issue in behavioural science. Moreover, this promotes transparency in reporting results and analyses, allowing for a better assessment of the strength of evidence for a claim. For example, here, were any alternative analysis pipelines attempted? Also, there were many sub-groupings of the animals and subsequent comparisons between them which all seemed post-hoc. On what grounds were these divisions made-were other divisions examined as well?

This is a repetition almost word for word of point (6) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(7) On p. 12 (Fig 4), there is an attempt to look at the impact of a rare, extreme event by plotting a measure of preference for the 10 trials before/after the rare, extreme event. In the human literature, the main impact of experiencing a rare, extreme event is what is known as the wavy recency effect (See Plonsky et al. 2015 in Psych Review for example, now cited). What this means is that there tends to there tends to be some immediate negative recency (e.g., avoiding a rare gain) followed by positive recency (e.g., chasing the rare gain). Typically, this refers to the specific option that yielded that outcome. First, as the other analyses do, the current analysis combines choice of the option that yielded the rare outcome with choice of other options, so that cannot directly assess the impact of the rare, extreme event on choice. Also, using a 10-trial window would thus obscure any impact of this rare, extreme event. There is mention of the very next trial, but an analysis that looks at the 10-trial time course trial-by-trial could reveal any impact that might be predicted from the human literature.

This is a repetition almost word for word of point (7) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(8) As I understood the method (p. 31), the assignment of options to physical locations was not random or counterbalanced, but deliberately biased to have one of the options in the preferred location. This would seem to create a bias towards a particular option and a bias away from the other options, which confounds the preference data in subsequent analyses. Table S4 reinforces this concern where the vast majority of response are clustered in the two most preferred options from training.

This is a repetition almost word for word of point (8) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(9) Are delays really losses? This is a big assumption. Magnitude and delay are different aspects of experience, which are not necessarily commensurable and can be manipulated independently. And, for the model, how were these delays transformed into outcomes for the model. Eq 1 skips over that. Is there an assumption of linearity? In addition, I was not wholly clear if the delays meant fewer trials in a session or if the delays merely extended the session and meant longer delays until the next choice period.

This is an exact repetition of point (9) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

Other points:

(1) I think the authors still misunderstand the concept of "hot-stove effects". The idea is that the experience of a very bad outcome can lead to avoiding the situation again (i.e., not sampling that option) and can provide the appearance of oversensitivity to that bad outcome. Here, that might be more thought as "black-swan avoidance". Imagine if, to the rat, all options are equal in value, then some initial bad luck in encountering the black swan might make the animal avoid that option, even though with enough experience, then it would have been equal in value.

This point is reminiscent of recommendation (5) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(2) I am still not convinced that the Jensen inequalities add to this paper in terms of understanding the rat behaviour. That may be more suited for a different paper about the statistical and mathematical properties of certain generative distributions, but not here given what rats actually choose and experience.

This point is reminiscent of recommendation (8) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(3) Providing the data open access is very good. The code, however, should be equally available and not just upon request. Code needs to be available for assessment during peer review and for reproducibility checks. There are substantial enough problems with reproducibility in the field that code availability should be a minimum criterion for publication (see Miske et al., 2026 in Nature for the most recent large-scale evaluation of this problem).

This point is reminiscent of recommendation (9) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(4) The paper still somewhat mischaracterizes the literature on rare events, posing it as a series of "exceptions", rather than recognizing that a huge chunk of the literature uses rare events rarer than 10%. Also, there is even existing terminology in that literature for exactly the situation that is being created here-rare treasures (aka jackpots here) and rare disasters (aka Black Swans here).

This is reminiscent of point (10) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(5) Defining the observed behaviour in terms convexity, instead of stating choices more plainly obscures what is done/found. This is especially the case here because convex and concave mean different things when applied to gains/losses in terms of whether or not that option can lead to the REE. The use of the terms obscures rather than clarifies and probably is best left for the discussion (and maybe the intro) when mapping from theoretical distributions to the experiment at hand. In the paper, even the bottom of p.5 seems to incorrectly define "Total Sensitivity" as the combined proportion of selecting convex options in either domain, which does not map how convex is defined in Fig 1B or elsewhere in the text.

This is reminiscent of point (3) appearing in your previous report, which as stated above we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

(6) Fig 1C is baffling. Why are probabilities drawn moving away from the origin? The standard scientific plotting convention is for numbers to grow when moving away from the origin. That would be vastly clearer. Also, the color coding is confusing. Green-red maps onto convex-concave, but that would naturally seem to indicate gains vs losses, not convex vs concave. And why are probabilities growing larger in both directions from the origin? Much more sensible to communicate the procedure would likely be a standard plot of magnitude vs probability.

As explained in the main text of the article, panel (c) in Figure 1 reveals an important and novel feature of the design: gains and losses are either convex or concave in decreasing probabilities, meaning that the gain/loss gets more rare, it becomes larger (if convex) or smaller (if concave) in a nonlinear fashion.

(7) Discussion: I think the main difference between the human situations discussed and this experiment is that humans have not experienced those rare "black swan" outcomes. Rather, they hear about the disasters that are possible and do not incorporate that information, as discussed in the description-experience literature already cited in this paper (though not in that context).

We thank the referee for pointing this out. However, it is not clear to us that the various trauma experienced in real life by humans do not share properties with Black Swans in our experimental design.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Small points:

- p. 4. Options are not strategies. Picking two out of the 4 options more often, is not picking two strategies. That's picking two options (also on p. 7, but really throughout).

This has been changed in the text.

- The sums don't add up in probability of outcomes. How were they 0.9, 0.1, 0.01? What were they exactly? What exactly is epsilon?

Exact probabilities, which of course add up to one, are given in Material and Methods (page 29).

- The term "one-sided sensitivity" to refer to the selection of options include rare-extreme outcomes is also confusing. There are many other words that might work better here, including "encounter", "choice", "selection", or even "preference".

One-sided Sensitivity if a proposed measure of the choice asymmetry, as explained in the text (pages 5-6, including caption of Figure 1).

- I don't think that Figure 3 is more intuitive. It's still a summed measure, with rats sub-divided into post-hoc groups. Also, aren't the groups divided precisely in part by the selections that are being shown in this plot?

There is no claim that Figure 3 is more intuitive. As explained in Material and Methods (pages 33-34), it provides an alternative way to represent behaviors (BSA/JPS vs TSREE/OSREE).

- Fig 3 has no black or dark and light grey. There is no one asterisk in the figure. The light grey is irrelevant because all bars must sum to 1. No error bars or equivalent on the plot.

Dark and grey bars sum to one but have a different interpretation, as explained in the text (pages 10-11). We have dropped the one asterisk reference.

- p. 14. Technicality, but alpha need not be bound at 1 for a convergent equation. It only needs to be bound at 2 (real maximum value). Above 1 (but below 2) would be a type of overcompensation that would also converge at same Q value.

The assumption that alpha is positive and bounded by one is common in the literature and is important for stochastic convergence. Assuming that alpha is between one and two has undesirable implications, beyond possible non-convergence, in particular that Q values may fluctuate.

- p. 24. What was the generative frequency (not experienced frequency). Not adequately explained. Less than half a percent of all outcomes? Of all times that the relevant choice was made. This is not explained.

The sequences used to generate gains and losse are detailed in the Supplementary Material.

- p. 4. Says 41 sessions, but methods say 40 (e.g., Fig 7 and surrounding text)

This has been corrected in the text.

- My understanding of Tables S5 and S6 is that the best models did not include REE in Q sub-values. That seems to be opposite to the textual conclusion.

As stated in Table 1 (page 15), which summarizes results in Tables S5-S6, the selected models for rats 3, 11, and 12 do not integrate REE while the selected models for rats 4, 16 and 20 integrate REE though Q values and REE decision weights. For most rats, REE are integrated in the selected models through the latter only.

- What are the parameters in Table S7? The full 8-parameter model? But how are these the ones selected by BIC as per caption? Also, there are a number of anomalous values-lots of 1s and 0s, plus a +40 on the value of the losses for Rat 20. Columns are always gain then loss except first column.

We report in Table S7 all estimated parameters for each rat, but only for the model selected by the BIC criterion (see Table S5). Admissible values for alphas include 0 and 1. All estimates have been checked for identification. The first and second columns have been switched to have gain first.

- Table S11 does not subdivide by option selected. So, we cannot tell if the rats actually experienced the outcome distribution associated with some options.

Given the large number of nosepokes generated by each rat, reporting all actual gains and losses would consume too much space. On the other hand, given that each option has only three frequent and rare values, it is expected that each will be experiences by each rat, in view of the choice frequencies reported in Table S2 (page 52).

Author response:

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

eLife Assessment:

The study provides an important advance towards understanding how spatial and temporal transcriptional programs are integrated to regulate lineage-specific chromatin and enhancer activation. The functional evidence is currently incomplete, but the current data provide a solid correlative and conceptual foundation. Functional experiments directly linking Gsb occupancy to chromatin state and regulation of some lineage-specific targets would further strengthen the causal interpretation of the model. Clarifying the scope of conclusions and explicitly acknowledging the technical limitations of current chromatin assays would provide a more balanced interpretation of the manuscript.

We thank the reviewers and editors for their comments on our manuscript. We address here the concerns raised by them.

Public Reviews:

Reviewer #1 (Public review):

Summary:

It has long been known that Drosophila embryonic ventral nerve cord neuroblasts incorporate both spatial and temporal transcription factor expression to generate 30 distinct neuroblasts and lineages per hemisegment. This manuscript aims to elucidate the mechanism by which this integration of spatial and temporal transcription factors occurs through "direct regulation" or "epigenetic regulation". Direct regulation is defined as both spatial and temporal factors binding to open chromatin and working together to dictate specific lineages. Epigenetic regulation is defined as a spatial factor priming the chromatin in a neuroblast-specific manner to allow for the integration of temporal factors to generate specific lineages. The authors conclude that there is a two-step model in which a spatial transcription factor code "primes" the chromatin in terms of accessibility and then recruits temporal factors to ensure lineage-specific enhancer activation.

We thank the reviewer for this clear and succinct summary and for accurately capturing the central idea of the model we propose. In particular, we appreciate that the reviewer highlights the distinction between the previously proposed “direct regulation” and “epigenetic regulation” models, which our work suggests may operate together within neuroblast lineages through a combinatorial spatial transcription factor code — a model we refer to as the “distributed STF code model”.

Strengths:

The authors tested two models, "direct regulation" vs "epigenetic regulation" in a well-defined pool of neural stem cells during normal development.

We thank the reviewer for recognizing this aspect of the study.

Weaknesses:

The data in this study cannot clearly substantiate these two models.

Overall, there are a number of issues that are inconsistent and not supportive of the model proposed in this manuscript. Firstly, there is no evidence of pioneer factor activity in any of the NB lineages described - i.e., any changes in chromatin accessibility being shown over time. The authors must show chromatin conformation changes during the window of spatial transcription factor expression in order to convince the readers of this phenomenon.

Thank you for raising this point. We agree that a developmental time course of chromatin accessibility would be very informative. The difficulty is that, in this system, the relevant sequence unfolds extremely rapidly and across two cellular contexts. Spatial transcription factors such as Gsb are expressed in the neuroectoderm; NBs then delaminate, and Hb expression begins almost immediately — on the order of minutes to tens of minutes. Before delamination there is no NB that can be targeted with lineage-specific drivers, whereas after NB formation the temporal program is already under way. This transition therefore cannot currently be resolved using lineage-restricted Dam profiling.

In most studies, however, pioneer or chromatin-priming activity is inferred from a transcription factor’s ability to bind regions of relatively low accessibility and alter accessibility in a heterologous cellular context, rather than from direct developmental timecourse measurements. Our study provides both types of evidence: Gsb occupies accessible and relatively less-accessible regions in NB5-6 (Figure 4), while ectopic Gsb expression in NB7-4 causes bidirectional chromatin remodelling, with corresponding changes in Hb occupancy (Figure 6 and Figure 6—figure supplement 2).

In light of this technical constraint, and in response to the reviewer’s broader concern, we have revisited our original interpretation. We now emphasise Gsb’s ability to alter chromatin accessibility bidirectionally and use the term “chromatin priming” rather than “pioneering.” We also make clear that Gsb does not act alone to establish the NB5-6 chromatin landscape, but functions within a broader, distributed STF code.

Some examples of relevant manuscript changes are:

- “We found, however, that Gsb’s role in chromatin remodelling was more complex: ectopic Gsb remodelled chromatin bidirectionally with regions both losing and gaining accessibility upon Gsb misexpression.”

- “Thus, Gsb’s chromatin-remodelling capacity is not equivalent to autonomous opening of lineage-appropriate enhancers. Rather, these data support a model in which Gsb contributes to chromatin priming as part of a broader NB-specific STF code…”

- “Thus, Gsb can engage loci and directly restrict chromatin accessibility at bound sites, but its ability to promote accessibility and Hb recruitment likely requires additional NB5-6-specific inputs.”

Secondly, the phenotypic data do not align with the sequencing data - the story would be more cohesive if the sequencing data and phenotypic data were in the same NB subtypes. On one hand, we are shown that Gsb misexpression induces loss of chromatin accessibility in NB 7-4, however in the widespread loss model, we are not shown a phenotype in these NB7-4 - which suggest that the chromatin accessibility at these sites (sites that have already been distinguished as SoIs for that NB subtype) does not play an important role in distinguishing NB 7-4 identity. However, the authors report loss of NB3-5 identity but have no evidence as to how the chromatin has changed (or if it has at all) in that subtype, leaving the readers to wonder how the loss of identity occurred

Thank you for raising this point regarding the alignment between the chromatin and phenotypic analyses. The reviewer’s comment made us realise that the rationale for these experiments may not have been sufficiently clear in the original manuscript and could therefore be perceived as misaligned. We therefore explain the logic of the experimental design here and have edited the manuscript to clarify this point for readers.

The chromatin experiments were designed to test whether Gsb is capable of remodelling chromatin when introduced outside its endogenous domain. NB7-4 provided a convenient heterologous context with clean genetic access for TaDa/CATaDa profiling.

Importantly, although NB7-4 was selected primarily for this technical reason, Gsb misexpression did affect NB7-4’s identity readout: at higher induction levels, the NB7-4-specific Gal4 reporter was lost. Because this same driver was required for lineage-restricted chromatin profiling, we titrated Gsb misexpression to a lower level that preserved reporter activity while still allowing us to assay chromatin accessibility and Hb occupancy. This calibration is documented in the new Figure 6—figure supplement 1. Thus, the calibrated profiling condition should not be interpreted as evidence that Gsb has no effect on NB7-4 identity; rather, it was necessary to retain genetic access to the lineage.

The phenotypic experiments addressed a different question: the developmental requirement for Gsb within its endogenous spatial domain. Our analysis was therefore centred on NB5-6. Gsb depletion caused loss of the NB5-6-specific Lbe reporter and the NB5-6 neuronal markers Ap and Eya, whereas Gsb misexpression produced a partial gain of these markers (Figures 7 and 8). The accompanying changes in row-3/NB3-5 markers emerged as an additional reciprocal phenotype, consistent with Gsb established role in specifying row-5/6 identity while repressing row-3 fates, rather than as an independent endpoint that we had selected.

Thus, the chromatin and phenotypic experiments are complementary: the NB7-4 experiment tests Gsb’s capacity to remodel chromatin in a convenient heterologous context, whereas the NB5-6 experiments establish its developmental function within its endogenous domain. We have revised the manuscript to make this distinction explicit.

Relevant edits made to manuscript:

“Having shown that ectopic Gsb remodels chromatin and alters Hb occupancy in the NB7-4 lineage, we next asked whether altering Gsb function changes NB lineage identity. The misexpression experiments described above had already shown that, when induced at high levels, Gsb misexpression turned off the NB7-4-lineage Gal4 reporter, consistent with Gsb suppressing NB7-4 identity at sufficient levels. In the chromatin-profiling experiments above, this was addressed by inducing lower Gsb misexpression levels that preserved Gal4 expression. Together, these observations suggested that Gsb misexpression can influence lineage identity as well as chromatin state. However, since NB7-4 is not an endogenous Gsb-expressing context, we turned to NB5-6 to test the developmental consequences of altering Gsb function.”

Reviewer #2 (Public review):

Summary:

This article by Bhattacharya et al. investigates how neural stem cells (NSCs, NBs) in Drosophila integrate spatial and temporal cues to activate neuron-specific terminal selector (TS) genes. Prior to this work, it was understood that NSCs utilize spatial transcription factors (STFs) and temporal transcription factors (TTFs) to determine lineage identity and birth order, but the mechanisms of integration were not fully elucidated. The authors employed chromatin profiling techniques to analyze the binding of STFs and TTFs in two specific neuroblast lineages, NB5-6 and NB7-4. They found that Gsb (an STF) binds both accessible and less-accessible chromatin in NB5-6, while En (another STF) binds only to pre-accessible chromatin in NB7-4. The findings support an "STF code" where the combination of pioneer and non-pioneer spatial factors, along with temporal factors, triggers neuroblast-specific enhancer activation and determines lineage identity.

We appreciate the reviewer’s careful summary of our findings and their clear articulation of the STF-code framework that emerges from the work.

Strengths:

The experiments are well-executed, the interpretations are generally sound, and the figures are clear and elegant. However, some conclusions are drawn too broadly without essential functional data. Therefore, additional work is needed to more effectively convey the central message.

We thank the reviewer for their positive assessment of the experiments, interpretation, and figures, and we respond to their specific concerns below.

Weaknesses:

(1) Integration of TaDa and functional data on Gsb for the STF model

The authors demonstrate that TaDa profiling maps Gsb binding across the genome and identifies candidate chromatin-priming sites in NB5-6. Gsb LOF/GOF experiments reveal effects on NB identity. Combining TaDa data with LOF and GOF analyses indicates that Gsb influences NB5-6 specification by binding to both open and relatively closed chromatin, helping maintain NB5-6 identity while limiting NB3-5 fate.

However, the study does not establish a direct link between specific LOF/GOF phenotypes and particular genomic targets. For instance, analyzing Gsb occupancy at lineage-specific identity factors or terminal selector genes (such as Lbe, Ap, or Eya for NB5-6; and Ems, etc., for NB3-5) in wild-type and manipulated conditions (Gsb misexpression) would directly connect chromatin binding to the regulation of fate determinants. These investigations would strengthen the mechanistic connection between the correlative TaDa profiles and the observed identity changes, supporting the idea that Gsb functions as a context-dependent chromatin-priming factor within the STF code, rather than as a generic transcription factor.

We thank the reviewer for this suggestion. We agree that examining Gsb occupancy at known lineage determinants helps connect the genome-wide TaDa profiles to the developmental phenotypes. We have therefore added browser profiles showing endogenous Gsb occupancy at several loci associated with NB5-6 identity and its neuronal output, including lbe, ap, and eya (new Figure 2E). These are the same markers that are lost following Gsb depletion and partially gained following Gsb misexpression (Figures 7 and 8), providing a locus-level connection between Gsb binding and the observed changes in NB5-6 identity.

The precise comparison suggested by the reviewer is difficult because the binding and misexpression experiments were necessarily performed in different contexts. Gsb occupancy was measured in NB5-6, where Gsb is normally expressed, whereas the effect of Gsb misexpression on chromatin was measured in the heterologous NB7-4 context where Gsb is not normally expressed. We therefore did not measure Gsb occupancy following its misexpression in NB7-4 and so cannot compare Gsb binding before and after misexpression at individual loci in NB7-4.

We have nevertheless added genome-browser examples showing how Gsb misexpression affects accessibility and Hb occupancy at lineage-associated loci (new Figure 6M). The ems locus provides one such example: ectopic Gsb reduces both accessibility and Hb occupancy at ems in NB7-4, while broad Gsb misexpression causes loss of Ems expression and of the independent NB3-5 reporter R59E09>GFP in the phenotypic experiments (Figure 8).

(2) Gsb misexpression reveals bidirectional chromatin remodelling

Experiments with ectopic Gsb expression demonstrate bidirectional chromatin remodelling in NB7-4, showing decreases in accessibility at some binding sites and increases at others. While the authors show that Gsb can disrupt chromatin upon misexpression, interpreting its "pioneer-like" or chromatin-priming activity is complex due to several factors: the misexpression occurs in a non-native lineage, the direct versus indirect effects rely on whole-embryo Dam-Gsb peaks instead of NB7-4-specific binding, and heat-shock-induced chromatin changes are not fully accounted for. These issues make it challenging to definitively determine Gsb's role in chromatin priming.

A complementary approach would be to perform Gsb knockdown/loss-of-function in its native NB5-6 lineage and profile chromatin accessibility (TaDa or CATaDa). This would allow a cleaner, more physiologically relevant assessment of Gsb's contribution to priming, SoI establishment, and Hb recruitment. Such an experiment would strengthen the causal link between Gsb occupancy and chromatin state and clarify whether Gsb truly acts as a context-dependent pioneer in vivo, rather than producing indirect effects due to ectopic misexpression.

We thank the reviewer for this thoughtful comment. The reviewer raises four related but distinct issues, which we address separately below.

(1) Gsb was misexpressed in a non-native lineage

As discussed in our response to Reviewer 1 regarding pioneer activity, expression in a heterologous cellular context is a standard experimental strategy for testing whether a transcription factor has the capacity to engage and remodel chromatin outside its endogenous setting. The use of NB7-4 was therefore deliberate: this experiment tested the sufficiency of Gsb to alter chromatin, rather than attempting to reproduce its physiological activity in NB5-6. Nevertheless, because Gsb produced bidirectional changes rather than autonomous chromatin opening, we have revised our interpretation. We now describe this experiment as demonstrating chromatin remodelling capacity and use “chromatin priming” rather than claiming a classical pioneer for its activity.

Relevant edits made to the manuscript: Results, Figure 7 and Figure 7—figure supplements 1 and 2.

(2) Direct and indirect effects were inferred using whole-embryo Gsb occupancy

We have not profiled Gsb occupancy directly in NB7-4 following its misexpression. However, we have now performed an unbiased genome-wide analysis using two independent Gsb-binding datasets: stage-matched Gsb occupancy from NB5-6 and whole-embryo Gsb occupancy. Since Dam methylation is cumulative across the window of Gal4 activity, the whole-embryo dataset serves as a proxy for embryowide sites that are compatible with Gsb occupancy. Across both datasets, the result was strikingly consistent. The set of 1,340 loci that lost accessibility upon Gsb misexpression showed strong Gsb occupancy in both datasets, whereas the 606 loci that gained accessibility showed little or no Gsb occupancy in either dataset (Figure 6E,H). Thus, two independently generated Gsb-binding maps systematically distinguish the loci that close from those that open.

This reproducibility — across many sites and two datasets — provides strong evidence that accessibility loss occurs at loci that Gsb can bind and is therefore likely to reflect a direct consequence of Gsb activity. Conversely, lower Gsb occupancy at sites that gain accessibility suggests that these gains are more likely to be indirect. The corresponding changes in Hb occupancy further strengthen this interpretation (Figure 6C–G).

In summary, we find it particularly compelling that two independently generated Gsb-binding maps, obtained at different developmental stages and in different cellular contexts, identify the same systematic distinction: loci that close upon Gsb misexpression are Gsb-bound, whereas loci that open are not. We therefore consider this a strong and unbiased result supporting a direct role for Gsb in chromatin closing.

Relevant edits made to the manuscript: (Results; Figure 6E, H)

“Although we did not directly profile Gsb occupancy in NB7-4 upon misexpression, we asked whether the sites that lose or gain accessibility differ in their propensity to be bound by Gsb. To do this, we mapped independent Gsb occupancy datasets onto these two classes of remodelled sites: stage-matched Dam: Gsb from NB5-6, where Gsb is normally expressed, and whole-embryo Dam: Gsb, which provides a broader map of Gsb-compatible loci. In both datasets, sites that lost accessibility upon Gsb misexpression in NB7-4 showed strong Gsb occupancy, whereas sites that gained accessibility showed little or no Gsb signal. Thus, the most direct consequence of ectopic Gsb is likely accessibility loss at loci that Gsb can bind, and this loss is accompanied by reduced Hb occupancy. By contrast, accessibility gains occur mainly at loci with little evidence of Gsb binding in independent datasets, suggesting that these gains are more likely indirect consequences of Gsb misexpression.”

(3) Heat-shock-induced chromatin changes were not fully accounted for

We agree that, because heat shock is required to induce Gsb, a contribution from the induction regime cannot be completely excluded. However, several observations argue that the chromatin changes are not dominated by a non-specific heat-shock response. First, the accessibility changes were reproducible across biological replicates (Figure 6—figure supplement 2). Second, as described above, sites that lost accessibility were consistently occupied by Gsb in two independent datasets and showed a corresponding reduction in Hb occupancy, whereas sites that gained accessibility showed little or no Gsb occupancy (Figure 6C–H). This structured relationship would not be readily explained by a general heat-shock response.

As an additional test, we performed a Gene Ontology analysis of genes associated with sites that gained accessibility. The enriched terms were predominantly related to development and cell-fate specification, including neuroblast differentiation and segment specification, while heat-shock and stress-response terms were not enriched (Author response image 1). Although none of these observations alone formally excludes an effect of heat shock, together they argue that the observed pattern reflects structured, Gsb-associated chromatin remodelling rather than a general stress response. We nevertheless interpret the accessibility gains cautiously as likely indirect effects of Gsb misexpression.

Author response image 1.

Gene ontology analysis of sites showing gain in accessibility upon Gsb misexpression in NB7-4. Genes overlapping the 606 sites showing at least 2-fold increase in accessibility (DamOnly signal) were annotated using the UCSC Table Browser (dm6). The resulting gene list was analysed for associated gene ontology (GO) terms using Metascape (Zhou et al. 2019). The top 20 enriched GO terms are represented as a bar chart, coloured by p-values.

(4) Chromatin accessibility following Gsb loss in NB5-6 would provide a more physiological test

We agree that this would be an informative experiment, and we explored several ways of perturbing Gsb early enough to address its endogenous function. A NB5-6-specific RNAi approach could not be used because the available NB5-6 Gal4 driver becomes active only after the period in which Gsb specifies the lineage.

The difficulty with conventional gsb mutants is different but equally limiting. Homozygous embryos would have to be identified during the brief developmental window in which Hb is expressed, while each TaDa/CATaDa replicate requires at least 30 mg of precisely staged embryos. The available fluorescent balancer markers are either not detectable at these early stages or become reliably detectable only towards the end of the window. It is therefore not feasible to identify and collect sufficient homozygous embryos — either manually or by fluorescence-assisted whole-embryo sorting — within the required time frame.

We therefore generated a gsb guide-RNA line and used Vasa-Cas9 to deplete Gsb in the early embryo. This strategy produced a high rate of Gsb editing, embryonic lethality and the expected axonal defects (Figure 7—figure supplement 1). When we examined NB5-6 in these embryos, we found that the Lbe-K reporter and the NB5-6 neuronal markers Ap and Eya were lost, confirming the requirement for Gsb in specifying this lineage (Figure 7).

Unfortunately, this also meant that we could not take the experiment forward for TaDa/CATaDa. Lbe-K-Gal4 is the driver we use to target NB5-6, and its expression was lost following early Gsb depletion. Without the driver, we can no longer restrict Dam expression to NB5-6 and therefore cannot obtain a lineage-specific chromatin profile. Thus, although the early CRISPR strategy allowed us to examine the developmental consequences of Gsb loss, the same experiment could not be used to assay chromatin accessibility in NB5-6. We have made this limitation explicit in the revised Discussion.

Relevant edits made to the manuscript: (Result, Figure 7 and Figure 7— figure supplement 1). We also now state explicitly in the “Scope and future directions” section that the current tools did not allow us to profile the chromatin consequences of Gsb loss directly in NB5-6 (Discussion).

(3) En is not a pioneer factor

The authors conclude that Engrailed (En) is not a pioneer factor, based on the observation that En binding correlates with accessible chromatin and that En is not enriched at NB5-6-specific SOIs. However, this conclusion is not sufficiently supported by the functional data.

First, the absence of En binding at NB5-6-specific SOIs does not necessarily indicate an inability to engage closed chromatin. These regions were not selected for the presence of En consensus motifs, so their lack of occupancy may simply reflect the absence of En binding motifs rather than a lack of pioneering capacity. A systematic motif analysis at NB5-6-specific SOIs is needed to determine whether En binding sites are present but unoccupied.

Second, the claim that En lacks pioneer activity relies solely on a single steady-state TaDa/DamID occupancy assay at one developmental stage. Because pioneer factor interactions can be transient, low-affinity, and stage-specific, such binding may not be detected by TaDa, which also depends on local GATC density and methylation kinetics and may yield false negatives. Given these technical limitations, the absence of En binding at less accessible regions does not definitively rule out a priming role.

In the absence of direct functional assays (En LOF/GOF), the authors should explicitly acknowledge these technical and conceptual limitations and tone down the claim that "En lacks pioneer activity".

We thank the reviewer for raising this point. We agree that the statement “En is not a pioneer factor” could be read as a general conclusion about En activity across developmental contexts. Our conclusion is more specific: in NB7-4 during the Hb-competence window, En occupancy is strongly biased towards pre-accessible chromatin and does not display the chromatin-engagement pattern expected of a pioneer factor. We have revised the manuscript throughout to make this context-specific interpretation clear. Below, we also address each of the reviewer’s points.

(1) The absence of En at NB5-6-specific SoIs could reflect an absence of En-binding motifs

We agree that the absence of En occupancy at NB5-6 SoIs would not be informative if these loci lacked En-binding motifs. We therefore performed the suggested motif analysis. En motifs were present at comparable frequencies in NB5-6- and NB7-4-specific SoIs (88.0% and 86.5%, respectively), with both enriched relative to matched shuffled controls (new Figure 3—figure supplement 1L). Thus, NB5-6 SoIs are motif-compatible but remain unoccupied by En in NB7-4. Their lack of En occupancy cannot therefore be explained simply by motif absence and instead points to additional determinants such as chromatin accessibility or cofactor context.

Relevant edits made to the manuscript: Result, Figure 3B–C and new Figure 3—figure supplement 1L)

“As expected, En was enriched at NB7-4-specific SoIs, where Hb uniquely binds in this lineage. However, there was no detectable En signal in NB7-4 at sites known to be NB5-6-specific SoIs, which remain relatively less accessible and Hb-free in NB7-4. This difference is unlikely to be explained simply by En motif availability, since En motifs are similarly represented at NB7-4- and NB5-6-specific SoIs. Thus, at SoIs, En occupancy is associated with the cognate, accessible NB7-4 SoIs, with little detectable occupancy at the non-cognate, relatively less-accessible NB5-6 SoIs.”

(2) TaDa may fail to detect transient, low-affinity or stage-specific En binding

We agree that no occupancy assay can exclude interactions below its detection threshold. However, TaDa is cumulative rather than a steady-state snapshot: Dam methylation accumulates during the expression window, allowing transient interactions to leave a detectable signal. Genome-wide, En occupancy was strongly weighted towards accessible chromatin, and accessibility predicted En binding with an AUROC of 0.74 (Figure 3E–I, Figure 3—figure supplement 2 and new Figure 3— figure supplement 3E).

Gsb provides an internal comparison using the same experimental framework. Gsb binding was detected at both accessible and relatively less-accessible chromatin, and accessibility did not predict Gsb occupancy better than chance (AUROC = 0.41; Figure 4E–I and new Figure 3—figure supplement 3E). This argues that the En pattern is not caused by a general inability of TaDa to detect binding at less-accessible loci. We nevertheless acknowledge that rare interactions, interactions below the detection threshold or binding outside the assayed window cannot be excluded. The resolution and cumulative nature of TaDa are now also described explicitly in the revised manuscript.

Relevant edits made to the manuscript: Result section for the genome-wide analysis and Discussion section for the TaDa limitations; Figure 3E–I, Figure 4E–I, Figure 3—figure supplement 2 and new Figure 3—figure supplement 3E).

(3) Direct functional assays of En were not performed

We agree that determining whether En actively establishes or maintains chromatin accessibility would require En loss- or gain-of-function experiments combined with chromatin profiling. These experiments were not performed in this study, and we have therefore removed the categorical statement that “En is not a pioneer factor.”

The revised manuscript now states the more specific conclusion supported by our data: En occupancy in NB7-4 during the Hb-competence window is strongly biased towards pre-accessible chromatin. We also acknowledge that the current experiments cannot exclude rare or transient interactions below the detection threshold, or chromatin-remodelling activity by En at other loci, developmental stages or cellular contexts. The factors that establish the NB7-4 accessibility landscape therefore remain unresolved.

Relevant edits made to the manuscript: (Result; Figure 3)

“Taken together, these results show that En occupancy is strongly biased toward preaccessible chromatin in NB7-4, including at NB7-4-specific SoIs. Thus, En is well placed to integrate spatial and temporal information through direct regulation at preaccessible enhancers. However, because NB7-4 has a distinct accessibility landscape, the factors that establish this landscape remain unresolved. We therefore propose that NB7-4 may use a combinatorial STF-code logic, in which other lineage-specific factors help establish NB7-4-specific SoIs, while En occupies this pre-accessible landscape and likely collaborates with Hb to activate lineage-specific enhancers.”

(4) Clarity of STF-code Model and Central Message

The manuscript begins by presenting two models, direct and epigenetic, but the central takeaway of the paper is not clear. Specifically, the nuanced roles of the spatial factors Gsb and En as chromatin-priming versus stabilizing/effector factors within an STF code, and the resulting division of labor, are not clearly illustrated. The distinction between Gsb as a chromatin-priming factor and En as a cofactor-dependent activator/stabilizer should be explicitly presented in a stepwise model for better clarity. The authors could strengthen this by providing a schematic with two sequential stages illustrating how neuroblast identity factors (STF code) change chromatin states to drive lineage-specific enhancer activation. The schematic can be shown from the neuroectoderm to individual NB lineages to make it more panoramic.

We thank the reviewer for this suggestion. This comment, together with related points raised below, made us realise that the manuscript did not bring out strongly enough that our data lead us to propose a third model: the distributed STF-code model. Rather than treating direct and epigenetic regulation as mutually exclusive alternatives, this model distributes these activities across different members of a NB-specific STF code. We have now revised the manuscript to reflect this transition. For example, we now state this explicitly in the Abstract, at the end of the Introduction and at the beginning of the Discussion.

Relevant edits made to the manuscript: Abstract, Introduction, Discussion, and have added a new summary schematic (new Figure 9).

(5) Identification of Priming Factors in NB7-4

While the authors suggest that an unknown priming factor might be responsible for establishing sites of integration in NB7-4, they do not identify or explore potential candidates for this role. Further investigation into what factors might be involved in chromatin priming in NB7-4 could provide a more complete understanding of the mechanisms at play.

We thank the reviewer for this suggestion. We agree that identifying the factors that establish the NB7-4 accessibility landscape is an important next step. Our current data do not identify such a factor, and doing so would require systematic perturbation of candidate STF-code members together with lineage-specific chromatin profiling.

We have nevertheless made this question more concrete in the revised Discussion. We identify Msh as a candidate shared input in NB5-6 and NB7-4, highlight additional candidates suggested by motif enrichment at NB7-4 SoIs, and propose NB6-4 — which coexpresses Gsb and En — as a useful context in which to test the division of labour between STF-code members. We present these as testable candidates rather than established priming factors.

(6) Functional Validation of STF Code Components

The study proposes an STF code for each neuroblast lineage, but the specific components of these codes, beyond Gsb and En, are not fully explored. Identifying and validating additional factors that contribute to the STF code in each lineage could strengthen the conclusions.

We thank the reviewer for this point. We agree that the complete composition of the NB5-6 and NB7-4 STF codes remains to be established, and we now make this explicit. The present study proposes a mechanistic framework based on the different chromatin-engagement properties of Gsb and En, rather than claiming to have defined or validated every component of either code.

As noted in our response above, the revised Discussion identifies Msh, Iroquois-complex members and TF families enriched at NB7-4 SoIs as candidate additional components. Testing these factors individually and in combination, with chromatin, Hb-occupancy and lineage-identity readouts, will be required to define the minimal functional code for each lineage. We present this as an important direction for future work (lines 759–770).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The reviewers appreciate the content shown in Figure 1, which is helpful for people who are unfamiliar with the system as a whole. One key issue is that later in the manuscript, the authors look at Gsb and describe it as a factor that works to close chromatin, making the model depicted in panel E misleading when reading the first half of the manuscript and leading to confusion/whiplash when getting to Figure 6, where a spatial transcription factor is thought to play a role in closing chromatin.

Thank you for pointing this out. Figure 1 was intended to present the two models currently proposed in the field and as the starting hypotheses for the study. It was not intended to present the conclusions from our study. We realise, however that this distinction was not clear and since we did not present the updated model, it made the later finding appear contradictory.

We have now made substantial edits to the text and have made the transition from the original models to our revised interpretation explicit in the Introduction and Discussion. We have also added a new summary model (new Figure 9), which shows that chromatin opening, chromatin closing and STF–Hb engagement can be distributed across different members of an NB-specific STF code.

(2) It is unclear what "less accessible" actually means. The reviewers would like to see quantitative standardization to define the degree of chromatin accessibility when using the Dam expression alone.

We thank the reviewer for this point. The comment made us revisit how we defined accessibility, which we had previously treated too much as a binary distinction between accessible and inaccessible chromatin. We have now revised our analyses to represent chromatin accessibility as a continuum of states.

We defined a common set of 27,119 DamOnly-marked regions across both NBs, ranked them by mean DamOnly signal and divided them into deciles from least to most accessible. The construction and validation of this continuum are shown in new Figure 2G and new Figure 2—figure supplement 2A–D. We also use this framework to examine STF occupancy and Gsb-dependent chromatin remodelling across the accessibility spectrum (new Figure 3— figure supplement 2A and new Figure 6—figure supplement 2E–F).

Where a discrete lineage-specific comparison was required, we applied a minimum two-fold difference in DamOnly signal between the NBs. This identified 845 NB5-6-preferential and 1,067 NB7-4-preferential regions. A region preferentially accessible in one NB is therefore described as relatively less accessible in the other, rather than as completely inaccessible.

Relevant edits made to the manuscript: Results, new Figure 2G and new Figure 2—figure supplement 2A–D.

(3) A key takeaway in Figure 3 is that En is binding already accessible chromatin. Another key point that this manuscript makes is that spatial-temporal factors (and codes) are responsible for this opening. We have not yet been shown that chromatin accessibility of this neuroblast identity actually changes upon spatial-temporal factor expression. I suggest including data of the dam-only control as a time course. Showing chromatin accessibility just before temporal factor expression and then after to validate that pioneer factor activity appears to be likely.

We appreciate this suggestion and agree that, conceptually, the model implies a temporal sequence in which spatial factors first act during neuroectoderm patterning and temporal factors such as Hb subsequently engage the chromatin after neuroblast formation. In practice, however, these events occur in very rapid succession during development. Spatial transcription factors are expressed in the neuroectoderm, neuroblasts are specified and delaminate, and Hb expression begins almost immediately after neuroblast formation — all within a short developmental window on the order of minutes to tens of minutes.

This makes it difficult to directly test chromatin accessibility changes across these stages using lineage-restricted Dam-based approaches. Before delamination there is no neuroblast to target with the available drivers, and once the neuroblast forms the temporal program is already underway. As a result, the sequential changes in accessibility that the reviewer is suggesting cannot currently be resolved with the available tools.

We agree that directly visualizing how chromatin accessibility changes during this brief developmental transition would be very interesting, but doing so would likely require approaches with much higher temporal resolution, such as live imaging-based methods for monitoring chromatin accessibility.

(4) Similar to the comment for Figure 3, showing chromatin accessibility changes in the NB subtype via a time course that includes both before and after spatial transcription factor expression begins.

This point is closely related to the reviewer’s previous comment regarding a temporal analysis of chromatin accessibility. Please refer to our response above describing the developmental timing and technical limitations that make such an experiment difficult in this system.

(5) It is difficult to reconcile the conclusion in Figure 5 that regions bound by both En/Hb or Gsb/Hb are considered the highest accessibility. Can the authors touch on the logic for this, given that in the next figure, they are going to suggest that Gsb works as a factor that is primarily responsible for closing chromatin? It is unclear how Gsb is closing chromatin, but it is also binding Hb, and in those regions, chromatin is most accessible.

We thank the reviewer for raising this point. The findings in Figures 5 and 6 may initially appear difficult to reconcile, but we think that they both actually point to the same conclusion: that Gsb’s effect on chromatin is context-dependent.

An important point is that Gsb binding is not restricted to a single chromatin state. In its endogenous NB5-6 context, it occupies both accessible and relatively less-accessible regions (Figure 4B–C, E–F). Its presence at accessible chromatin does not establish that Gsb opened that chromatin nor that it closed it because these occupancy data do not reveal the direction of chromatin change. From these data we can only conclude that sites co-bound by Gsb and Hb are more accessible than sites bound by Gsb alone, suggesting that the outcome of Gsb binding depends on the surrounding regulatory context. In the presence of Hb — and likely other members of the NB5-6 STF code — Gsb can participate in a highly accessible, productive regulatory state (Figure 5C–E).

The misexpression experiment helps us interpret these relationships in the endogenous context. When Gsb is introduced into NB7-4, sites that lose accessibility are strongly Gsb-bound in two independent datasets, and this loss is accompanied by reduced Hb occupancy (Figure 6C–H). Some Gsb-bound sites also gain accessibility, consistent with bidirectional remodelling, but Gsb occupancy is negligible at these gain sites. Thus, outside its normal NB5-6 regulatory environment, the more direct effect of Gsb binding is likely chromatin closing.

This provides a possible explanation for the endogenous (NB5-6) data in Figure 5. The lower accessibility of sites bound by Gsb alone may reflect this closure-biased activity, whereas the highly accessible state at Gsb–Hb co-bound sites is likely to arise from the broader NB5-6 regulatory context. We do not conclude that every Gsb-only site is actively closed, or that Gsb itself opens the co-bound sites. Rather, our data suggest that Gsb can participate in different chromatin states, with the outcome of its binding shaped by Hb and other members of the STF code.

We have revised the Results and Discussion to make this interpretation clearer.

(6) The most striking piece of data from Figure 6 is that it appears the physiological role of Gsb is to reduce chromatin accessibility and that opening chromatin is an indirect effect. I am not sure that the field widely recognizes closing as chromatin as "pioneer-like" activity. Moreover, this finding seemed very out of place given the way the story has been sold thus far - discussing "priming of chromatin" and referring to this as opening in figure 1 and discussion of binding of these factors at open and less accessible.

Thank you for raising this issue, which overlaps with the reviewer’s previous point. We were equally struck by the result from Figure 6: the sites that lose accessibility are more consistent with a direct effect of Gsb, whereas the sites that gain accessibility are more likely to represent indirect effects. This suggests that Gsb can remodel chromatin bidirectionally.

We agree that the field does not generally describe chromatin closing as pioneer activity. We therefore no longer refer to Gsb as a pioneer factor. Instead, we describe Gsb as having bidirectional chromatin-remodelling capacity and refer to it as “chromatin priming” activity.

Finally, we agree that the original presentation made this progression difficult to follow. Figure 1 presents the two existing models as the starting point, whereas our data lead us to propose a third, distributed STF-code model. We now make this transition explicit throughout the revised manuscript and have added a new summary schematic (new Figure 9; See Results and Discussion).

Reviewer #2 (Recommendations for the authors):

Minor comment:

(1) Have the authors validated the specificity of the Lbe-GAL4 and 19B03AD;18F07DBD drivers? It is important to clarify whether these drivers label only NB5-6 and NB7-4 neuroblasts or also their progeny. Since the interpretation of chromatin dynamics is in the context of neuroblasts, reads from differentiated neurons could affect the conclusions.

We thank the reviewer for raising this point. These driver lines were extensively characterised in our previous study and are highly specific to the NB5-6 and NB7-4 lineages, respectively. Importantly, as the reviewer points out, they are not neuroblast-exclusive and also label progeny. Because our profiling is restricted to the early Hb competence window, this contribution should be limited to a small number of GMCs and the earliest-born neurons.

On rereading the manuscript, we realised that there were several instances where we used “NB-specific” too loosely when referring to these datasets. We have therefore revised the manuscript throughout to make clear that the TaDa/CATaDa profiles represent the NB5-6 and NB7-4 lineages during the Hb window and are not exclusively derived from the neuroblast itself. We have also added this explicitly as a limitation in the Scope and Future Directions section. Importantly, this does not change the essence of our conclusions, which are based on comparisons between these two defined lineages and on perturbations examined within the same lineage-restricted framework.

Relevant edits made to the manuscript:

- “The driver lines were previously validated as being specific to these lineages”.

- “First, the lineage-specific Gal4 drivers also label the immediate progeny of each NB; thus, although profiling was restricted to the early Hb competence window, when only a small number of GMCs and early-born neurons are present, the resulting profiles are not exclusively derived from the NB itself.”

(2) The lineage NB6-4 co-expresses both Gsb and En and represents an informative intermediate case. This context supports a cooperative STF-code model in which Gsb provides chromatin priming while En acts as an effector or stabilizer, without requiring autonomous pioneer activity. The authors should briefly discuss how NB6-4 fits into their model and whether Gsb priming in this lineage enables En-Hb co-occupancy and enhancer activation.

We thank the reviewer for this comment. We agree that NB6-4 is an especially interesting case in the context of our model, because it co-expresses both Gsb and En and therefore may provide a lineage in which both aspects of the proposed two-step mechanism can be examined together: Gsb could contribute to chromatin priming and En could function at already primed enhancers together with Hb. We now include this explicit example in the Discussion section.

(3) The authors' data support a role for Gsb in lineage-specific chromatin priming, but the functional experiments reveal important limitations. Gsb alone does not efficiently open closed chromatin, install NB5-6-specific SOIs, or recruit Hb, and ectopic Gsb often antagonizes native chromatin states. Thus, the results do not support Gsb as a classical standalone pioneer factor, as implied in the discussion. The authors should replace the term "pioneer-like potential or activity" with "context-dependent pioneer activity" in the results, as they have rightly mentioned in the discussion.

We agree with the reviewer. As discussed in our responses to the related comments above, our data do not support describing Gsb as a classical pioneer factor. Gsb remodels chromatin bidirectionally, with both gains and losses of accessibility, whereas pioneer activity is traditionally associated with chromatin opening. We have therefore gone further than the reviewer’s suggested change: throughout the manuscript, we have replaced “pioneer-like potential/activity” and “context-dependent pioneer activity” with “context-dependent chromatin remodelling” or “chromatin priming.” The Results and Discussion now make it clear that Gsb’s activity depends on the surrounding STF and cofactor context rather than representing autonomous pioneer activity.

(4) The use of ectopic expression systems may introduce artifacts or off-target effects that could affect the interpretation of the results. These potential limitations are not extensively discussed.

We agree that ectopic expression can produce indirect or non-physiological effects. The Gsb misexpression experiment was designed to test whether Gsb is sufficient to remodel chromatin in the heterologous NB7-4 context, rather than to reproduce its endogenous function in NB5-6. We therefore do not interpret every change in accessibility in the misexpression experiment as a direct or physiological role for Gsb in NB5-6. However, the changes are not random. Sites that lose accessibility are strongly associated with Gsb occupancy in two independent datasets and they also lose Hb occupancy, whereas sites that gain accessibility show little Gsb occupancy and are therefore more likely to reflect indirect effects (Figure 6C–H). The changes were reproducible between replicates, and genes associated with accessibility gains were not enriched for heat-shock or stress-response terms (Author response image 1). These analyses do not remove the limitations of ectopic expression, but they help distinguish the more likely direct effects from indirect ones. We now make both the purpose and the limitations of this experiment explicit in the Results and Discussion.

(5) The moderate correlation (0.7-0.82) between Dam-En and Dam-only reflects the expected overlap of En binding with accessible chromatin, but it also underscores a limitation: TFs that prefer open regions may show high baseline similarity to Dam-only, potentially masking low-affinity or transient interactions. The authors should acknowledge this when concluding that En lacks pioneer activity.

We thank the reviewer for bringing this up. We want to clarify that our conclusion that En preferentially occupies accessible chromatin is not based only on the moderate genome-wide correlation between Dam: En and DamOnly. We also examined En binding at defined SoIs and at differentially accessible loci across the genome. In both analyses, En is strongly enriched at accessible NB7-4 sites but shows little detectable enrichment at the corresponding less-accessible sites (Figure 3B–F). We have now extended this analysis across 27,119 regions ranked along the full accessibility spectrum. Here too, En signal remains low across the less-accessible bins and increases principally in the most accessible bins (new Figure 3— figure supplement 2E).

A useful comparison here is Gsb. Using the same experimental and analytical framework, we readily detect Gsb binding at both accessible and relatively less-accessible chromatin in NB56 (Figure 4B–F; new Figure 3—figure supplement 2E). Thus, the method is able to detect binding at less-accessible chromatin when it occurs. Consistent with this, accessibility predicts En occupancy but not Gsb occupancy in the corresponding ROC analysis (new Figure 3—figure supplement 3E). We also refer the reviewer to our response to the related comment above, where we discuss this comparison in more detail.

Finally, we want to point out that TaDa is not a snapshot assay. Dam-mediated methylation accumulates over the expression window and across many cells, so repeated weak or transient interactions should, in principle, contribute to the signal. We agree, however, that very rare interactions below the detection threshold cannot be excluded. We have therefore tempered our conclusion throughout the manuscript: rather than stating that En lacks pioneer activity, we now conclude that En occupancy during the NB7-4 Hb window is strongly biased towards pre-accessible chromatin.

(6) The schematic illustrating the NB 5-6 and NB 7-4 SOIs (Figures 3A, 4A, and S2A) should be made clearer. When Hb is bound, sites that are accessible serve as SOIs for a specific lineage, whereas Hb-unbound, inaccessible sites do not. The authors can visually represent this by showing that, in the case of Hb binding, the accessible region functions as a resident SOI for the NB7-4 lineage, while the same region in NB5-6, being Hb-free, is inaccessible. This distinction could be indicated with a shaded or shadowed area from top to bottom in Figures 3A and 4A.

We thank the reviewer for pointing this out. We have revised these panels to make the visual distinction between lineage-specific SoIs and the corresponding Hb-free, less-accessible loci in the other lineage more explicit.

(7) At 472, change "Fig.S6C-F" to "Fig.S6C-D".

Thank you for spotting that!

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript the authors study the distribution of the KMT2A methyltransferase across the human ribosomal gene loci (rDNA) and the effects of its depletion on rDNA chromatin modification using a KMT2A conditional cell line. They used ChIP mapping data and claim to show that KMT2A depletion does not affect H3K4me3 levels but does reduce acetylation of H3K9 and reduces PCAF (KAT2B) binding. They further claim that KMT2A depletion causes stalling of RNA Polymerase I at the upstream "Spacer" promoter duplication on the rDNA.

Weaknesses:

I found the manuscript very confusing. In particular, I found it short on short on experimental detail and I found the data in general to be unconvincing. It is my opinion that the authors overinterpret their data, leading to unrealistic and unsupported claims. The manuscript also avoided discussing relevant recent studies on the regulation of the rDNA and of rDNA chromatin, most citations being to data 15 to 20 or more years old. This is most apparent when discussing the factors such as UBTF and SL1 that determine preinitiation complex assembly and the status of active versus inactive rDNA chromatin. Both have seen significant advances in recent years, and these should be thoroughly discussed.

Specific comments:

The authors do not describe the generation of the KMT2A conditional HEK293T cells or their treatment. Since these cells form the basis for subsequent experiments, they must be explained fully. I found that the conditional cell line had already been used in a previous unrelated publication "Chinchole et al. 2022". This manuscript explained that the KMT2A knockout is induced via Dox-controlled Cas9 in a HEK cell clone constitutively expressing guide RNAs to KMT2A. The KMT2A knockout requires a 7-day treatment with Dox, leaving wide open the question of direct versus indirect effects of KMT2A loss, and perhaps explaining some of the discrepancies with published data.

We thank the Reviewer for their comment. As the Reviewer correctly states, these KMT2A knockouts have been used in previous studies: Chinchole et al., 2022; PMID: 36111497 and Malik et al., 2023; PMID: 37379335. In both cases, the generation of KMT2A inducible knockout was described in detail in the Methods section; hence, in this manuscript we referred to these publications. However, if the Reviewer feels that details should still be provided, we will do so again here.

As the Reviewer is aware, KMT2A is an essential chromatin-bound protein, which is quite stable in its heterodimer form. As we described in our publication, Malik et al., 2023, the inducible knockout clones were obtained after extensive screening and thoroughly characterized. While the protein diminishes in the WB after 3 days, we thought it necessary to confirm that it does not persist on the chromatin in ChIP assays.

We are pasting the excerpt from the manuscript describing the relevant section below.

“Our initial attempts to generate MLL knock-outs in several different cell lines were not successful. Therefore, keeping in mind that MLL is essential for cell viability and growth [26,27], we generated and successfully obtained knock-outs in HEK-293 cell lines using doxycycline-inducible Cas9 expression vectors ([52]; Fig 3A). MLL levels were drastically reduced in the 2 independent MLL-knock-out clones shown here (MLL iKO#11 and iKO#20) and both KOs showed cell cycle profile similar to Control cells (S3A Fig). In the case of chromatin-binding proteins, often cellular levels show reduction but not the chromatin-bound fraction. We, therefore, confirmed that MLL chromatin binding was indeed reduced in our inducible knock-out cell lines by ChIP assays (Figs 3B and S3B), both on centromere and HOXA9 promoter”.

Inducible Cas9-mediated knockout provides an opportunity to generate irreversible knockouts, allowing sufficient time to deplete stable proteins and reveal delayed phenotypes or compensatory responses [PMID: 29036671]. However, this advantage has to be balanced with the potential secondary effects arising from prolonged depletion. Indeed, inducible Cas9 knockouts have been generated after similar induction periods by other laboratories to deplete chromatin-bound proteins [PMID: 28216383; PMID: 37702151], especially for members of the KMT2 family [PMID: 40846851, PMID: 27535106; PMID: 37535603 ]. Further, we have not observed any discrepancy with published data for KMT2A.

In mapping the interactions of KMT2A across the rDNA by ChIP they use 18 PCR amplicons, some of which the authors inaccurately state as targeting specific rDNA elements. For example, they state Primers (that is, Amplicons) #1-3 target the spacer and core 47S promoters. In fact, amplicon #2 overlaps neither of these promoters and lies centrally within the 1kbp of enhancer repeats between them. Exactly why emphasis is put on KMT2A chipping at these two promoters is anyhow questionable since KMT2A levels (Figure 1) appear equally high at multiple IGS amplicons.

As the enhancer repeats (ER) are clearly shown in the schematic of Fig. 1A and SF1B, and the same is stated in the legend of SF1B, rather than an inaccuracy, it is a matter of oversight. We thank the Reviewer for noticing this and bringing it to our attention. We will correct it in the text.

We thank the Reviewer for raising this point regarding our focus on the promoters in the present study and the binding of KMT2A to the IGS region. KMT2A’s role in regulating RNA polymerase II transcription by regulating gene promoters is well established. However, its role in regulating RNA polymerase I transcription at the rDNA promoter has not been characterized. In this study, we provide evidence for a previously unrecognized role of KMT2A in regulating rDNA transcription and hence extend its function to regulation of RNA polymerase I.

We agree that our ChIP data show KMT2A occupancy at multiple regions within the IGS, in addition to the promoter regions. For this reason, we felt it was important to present these data and perform ChIP-seq analyses of the rDNA locus to reveal the complete picture.

Our emphasis on the promoter regions is aimed at understanding the potential role of KMT2A in regulating RNA polymerase I transcription initiation. However, we recognize that the enrichment of KMT2A at multiple IGS regions raises the possibility that it may have additional functions beyond promoter regulation. We are currently investigating the role of KMT2A at the IGS, and in our future studies we hope to address the functional significance of this occupancy in greater detail.

Discrepancies with published data are particularly apparent in their mapping of H3K4me2, H3K4me3 and H3K9ac, all directly relevant to their conclusions. These modifications have been shown in several publications to map to a single major site a few hundred bp upstream of the spacer promoter in multiple human and mouse cell types. Since the authors fail to monitor H3K4 methylation and H3K9 acetylation at this dominant site they also fail to provide significant evidence that KMT2A in fact affects H3 methylation or H3 acetylation on the rDNA.

We thank the reviewer for raising this important point about the distribution of histone modifications at the rDNA locus and how they depend on KMT2A. Previous studies have established that active histone modifications are enriched at specific regions of rDNA. In particular, landmark studies from two groups have pioneered the use of genome assemblies to map these histone modifications. The Scacheri group [Zentner et al. 2011, PMID: 21355038] reported enrichment of H3K4me2, H3K4me3, and H3K9ac at the human rDNA promoter, along with additional active-chromatin-associated enrichment within the intergenic spacer. Subsequently, the same group demonstrated that the distribution of histone modifications in mouse embryonic stem cells differs from that in human embryonic stem cells and other differentiated mouse cell types [Zentner et al. 2014, PMID: 24347625]. These findings underscore the importance of examining the relevant regulatory regions in the appropriate biological system.

Similarly, studies from the Moss group radically redefine our understanding of how histone modifications are distributed across rDNA in mammals. They demonstrated that active histone modifications (including H3K4me2/3, H3K9ac, H3K27ac, and H3K36me3) are not present at the core 47S promoter or along the transcribed gene body of active rDNA repeats, but are instead strictly sequestered to a highly localized "Enhancer Boundary Complex" located a few hundred base pairs upstream of the spacer promoter. Consequently, this precise upstream hub represents the sole site of active histone modifications on active rDNA genes [Herdman et al., 2017, PMID: 28715449 ; Mars et al., 2018, PMID: 29158335]. These findings challenge the classical models of histone modification distribution at rDNA.

However, an extensive body of classical literature presents a complementary view where active histone modifications directly decorate the core 47S promoter and proximal transcribed regions to dynamically coordinate RNA Polymerase I transcription. Work from the Grummt and Santoro laboratories established that unmethylated, active rDNA repeats possess prominent H3K4me3 and hyperacetylated histones directly at the core 47S promoter, serving as a functional "poised" platform for pre-initiation complex (PIC) assembly [Santoro and Grummt, 2002, PMID: 12368916; Santoro and Grummt, 2005, PMID: 15767661; Mayer et al., 2006, PMID: 16678107; Schmitz et al., 2010, PMID: 20952535]. Furthermore, tracking chromatin remodelling complexes—such as the CSB-PCAF complex investigated by the different groups—has shown that active depletion of histone acetyltransferases leads to a direct loss of H3K9ac specifically at the primary 47S initiation site, causing a failure in Pol I loading [Shen et al., 2013, PMID: 23667505; Vintermist et al., 2011, PMID: 21559432]. Besides these reports, a wealth of independent functional data highlights that key chromatin regulators dynamically target and modulate the core 47S promoter region to dictate ribosomal transcription initiation. Some examples are referred to here [Xei et al., 2012, PMID: 22570494; Wang et al., 2011, PMID: 21960006; Zhu et al., 2010, PMID: 20531378; Frescas et al., 2007, PMID: 17994099].

Our investigation of KMT2A directly builds upon this functional promoter-centric model. While we appreciate that mapping variations exist between custom rDNA reference models in the literature, our data show clear and reproducible levels of H3 methylation and acetylation dynamics across the primary regulatory sites (including the 47S promoter and adjacent transcribed unit) upon KMT2A depletion. These changes correlate directly with functional changes in 47S pre-rRNA output, supporting a model where KMT2A-mediated histone modifications operate directly at the core transcription initiation machinery to regulate overall nucleolar output.

We acknowledge that the distribution of histone modifications across the rDNA repeat and their functional dependence on KMT2A represent distinct questions. Accordingly, we interpret the ChIP-seq profiles in conjunction with our site-specific ChIP-qPCR and functional experiments rather than relying exclusively on the genome-wide mapping data. We therefore conclude that our results support a role for KMT2A in regulating the acetylation-associated chromatin environment and transcriptional activity of the rDNA promoter, without claiming that KMT2A depletion reduces all active histone modifications across the locus.

We will clarify the relevant analysis and the scope of our conclusions in the revised manuscript.

The KMT2A deletion drastically reduces PolI and UBF (UBTF) engagement across the rDNA, and consistent with this, SL1 and RRN3 engagement is reduced as are 47S levels. Thus, whatever the 7-day KMT2A deletion is doing to the cells it is certainly inducing a very significant shut-down of active rDNA. How such an extreme experimental model can tell anything of KMT2A functions is unclear.

We feel that this concern is on similar lines as that stated in comment 1. We have already explained our inducible knockout model above. The cell-cycle profile of KMT2A-inducible knockout (iKO) cells reported in Malik et al. (2023), PMID: 37379335. provides relevant context for interpreting these effects.

We further wish to highlight that contrary to expectation, the H3K4me2/3 levels are largely unaffected on the rDNA in KMT2A iKO cells, which is surprising but not unexpected given the role of KMT2A in selectively trimethylating specific gene loci (PMID: 19703992). However, the loss of acetylation on H3 is very specific to the study at hand.

Unchanged H3K4me2/3 levels, along with selectively decreased acetylation, have not been reported for a general shutdown of active rDNA under extreme conditions like serum starvation etc. In case of a non-specific effect, both active methylation and acetylation marks are expected to go down. The presence of the H3K4me2/3 mark in our iKO cells acts as an internal control, confirming that the loss of H3 acetylation is a direct consequence of KMT2A depletion.

Furthermore, in the current manuscript, the effects of KMT2A deletion on the Pol I transcriptional machinery can be rescued by the KMT2A catalytic point mutant carrying the N3906A mutation but not by the mutant with TAD deletion. This rescue provides important evidence that the phenotype is linked to a specific function of KMT2A rather than being a nonspecific consequence of KMT2A deletion.

Our findings, considered alongside Lone et al. (2026) PMID: 42096476, support distinct roles for KMT2A and KMT2F in regulating rDNA transcription. In particular, the effects of KMT2A loss occur without a substantial reduction in rDNA H3K4me3, distinguishing its role from the H3K4me3-dependent function of KMT2F in promoting Pol I pre-initiation complex formation.

In the last results section, the authors further claim "Loss of KMT2A results in a stalled RNA Pol I complex at the spacer promoter" (Figure 4 and S4). To support this the authors try to map spacer promoter transcripts but mistakenly claim that the amplicon #1 can detect these transcripts. In fact, this amplicon overlaps the Spacer Promoter initiation site and so could not detect transcripts coming from this promoter. Published data, not cited, have demonstrated that PolI stalling at the spacer promoter occurs as a normal phenomenon on the active rDNA. Its loss is associated with suppression, not the opposite as inferred in this manuscript.

We thank the Reviewer for raising this point. We have double-checked that amplicon #1 is downstream of the spacer promoter start site. However, since the reviewer has raised this point, we will look into it in greater detail and remap our amplicons. We will also revisit the previous literature and compare our results with the published findings.

Reviewer #2 (Public review):

Summary:

This important manuscript presents solid evidence that the major contribution of KMT2A to ribosomal gene transcription is through promoting histone acetylation rather than H3K4 methylation. It is suggested this occurs in part through interactions of KMT2A with PCAF.

Strengths:

This manuscript advances an important concept that chromatin-modifying enzymes can also function to promote transcription through interactions with other transcriptional regulators independently of their catalytic functions. The data are overall supportive of this conclusion for KDM2A.

Weaknesses:

(1) Care needs to be taken regarding interpreting the lack of effect of depleting KMTs or HATs on histone acetylation or methylation levels. There are several overlapping HATS or KMTs that generate these modifications. The most that can be said from these negative results is that the depleted HAT or KMT is not the sole enzyme generating these modifications at these loci.

We thank the Reviewer for this important comment. We agree that histone modifications are regulated by multiple enzymes with overlapping or partially redundant activities, and that the absence of a detectable change following depletion of an individual KMT or KAT does not exclude a contribution from that enzyme to the regulation of the modification.

Specifically, the lack of a detectable reduction in H3K4me3 following KMT2A depletion indicates that KMT2A depletion alone is insufficient to produce a detectable decrease in H3K4me3 under the conditions examined. The persistence of this mark may reflect the activity of other KMTs and hence functional redundancy. In contrast, our observation that KMT2A depletion reduces H3K9 acetylation, together with our findings implicating PCAF in KMT2A-dependent rDNA transcription, supports a role for KMT2A in regulating an acetylation-associated mechanism at this locus.

Nevertheless, we acknowledge that these findings do not, by themselves, establish that PCAF is the sole enzyme responsible for H3K9 acetylation or that it accounts for all KMT2A-dependent effects on rDNA transcription. We will revise the interpretation of our results to avoid attributing the maintenance or loss of a histone modification exclusively to a single enzyme.

(2) The biochemistry supporting an interaction between KDM2A and PCAF is under-developed and not strong enough to support this conclusion at this point.

We thank the reviewer for their comment. Based on these comments and those from Reviewer 3, we plan to add more experiments to strengthen the KMT2A-PCAF interaction, including a reverse pull-down.

(3) It is concluded that acetylation causes increased rDNA transcription. However, acetylation may be a consequence of transcription instead, especially over transcribed regions.

We thank the reviewer for raising this important point regarding the relationship between histone acetylation and rDNA transcription. We agree that increased histone acetylation over transcriptionally active regions may either contribute to transcriptional activation or result from ongoing transcription. These possibilities are not mutually exclusive.

Our study provides several lines of evidence supporting a functional relationship between KMT2A and PCAF-associated histone acetylation, which indicate that acetylation is the cause and not a consequence of rDNA transcription. KMT2A depletion reduces rDNA transcription and is accompanied by a reduction in H3K9 acetylation. In addition, we present a model in which KMT2A facilitates the transfer of RNA Pol I PIC from the spacer promoter to the 47S promoter following its assembly at the spacer promoter by recruiting PCAF to rDNA through its TA domain. Together, these observations support that acetylation supports efficient rDNA transcription

Nevertheless, we acknowledge that these findings do not completely exclude the possibility that some of the observed reduction in histone acetylation occurs downstream of reduced transcription and will modify the discussion accordingly.

(4) Some conclusions, for example implicating PCAF, are based on overexpression experiments that are very artificial and difficult to draw conclusions from.

We thank the reviewer for their comment. We agree that overexpression experiments can produce non-physiological protein levels and potentially influence experimental readouts. However, our interpretation of PCAF involvement is based on a broader set of observations presented in this study, including the effects of KMT2A depletion on rDNA transcription and histone acetylation, together with our experiments examining the contribution of individual histone acetyltransferases to rRNA synthesis. These findings identify PCAF as a key co-activator of KMT2A-dependent transcriptional activation.

Therefore, the overexpression experiments have been used to provide mechanistic support rather than definitive evidence that endogenous PCAF is the sole or essential mediator of this process.

(5) Several figures are generated using publicly available data sets that were reanalyze using updated reference genomes, sometimes from different cell lines/types. This seems to be a useful exercise but the methods should include information regarding the robustness of these data sets.

We thank the Reviewer for their concern; we will update this information in the Methods.

Reviewer #3 (Public review):

Summary:

This manuscript examines a key mechanism by which KMT2A regulates RNA polymerase I transcription at ribosomal DNA. The authors suggest that KMT2A facilitates the recruitment of PCAF to rDNA. This process enhances histone acetylation and supports assembly of the RNA polymerase I transcription machinery. The study addresses an intriguing question by proposing a catalytic-independent role for KMT2A in rDNA transcription, potentially linking the KMT2A-dependent pathway to histone acetylation. However, several aspects of the proposed mechanism require further experimental validation. Notably, while the current evidence demonstrates associations among KMT2A, PCAF occupancy, histone acetylation, and rRNA transcription, it does not fully support the proposed objectives.

Strengths:

This could be the first report of a lysine methyltransferase regulating an acetyltransferase in Pol I-mediated gene expression.

Weaknesses:

(1) The causal relationship between KMT2A and the recruitment of PCAF needs to be demonstrated. Simply showing reduced PCAF occupancy after depleting KMT2A does not, on its own, prove direct recruitment. The authors should investigate whether KMT2A and PCAF physically interact, and whether this interaction depends on DNA or RNA.

As we have shown that KMT2A and PCAF interact by endogenous IP (Fig. S4D) and pull-down (Fig. S4E) experiments with the KMT2A C-terminal fragment containing the TAD domain, does the Reviewer mean in vitro interaction? Both proteins are large and may be difficult to produce in bacteria.

We do plan to perform reverse IP as suggested by Reviewer 2, and during these experiments, we can plan to test if this interaction is promoted by DNA or RNA by testing it in the presence or absence of DNase or RNase.

(2) The main prediction of the model is that restoring PCAF activity should reverse the molecular effects caused by the depletion of KMT2A. The authors should test whether PCAF restoration can mitigate the consequences of KMT2A loss. They should also assess PCAF occupancy, H3K9 acetylation levels, Pol I occupancy, and nascent rRNA synthesis.

We agree with the Reviewer that this is the central hypothesis of our study. Ideally, a simple global restoration or overexpression of PCAF should be able to rescue the effects caused by the depletion of KMT2A. However, based on our model and existing literature, we expect the following issues:

(1) We propose that KMT2A serves as a recruiter, a physical scaffold, to target PCAF to the rDNA. Therefore, mere overexpression of PCAF, in the absence of KMT2A, will not be able to ensure its localisation to the rDNA locus.

(2) Transcription activation by KMT2A involves tight synergy between its TA domain and specific KATs (PMID: 24253305; PMID: 31515273). The KMT2A TAD contains intrinsically disordered regions that must directly engage co-activator docking sites—specifically interacting with domains like the KIX domain of p300/CREB-binding protein acetyltransferase complexes—to transition into a stable secondary structure and drive downstream chromatin remodelling. Because this functional synergy requires the physical presence of both the KMT2A TAD and the KAT complex at the promoter, in our opinion, restoring PCAF activity in a KMT2A-depleted background cannot rescue localized H3K9 acetylation at the rDNA promoter. While we are not sure how PCAF engages with the KMT2A TAD domain, based on the above literature, the physical presence of KMT2A may be required.

We will test this hypothesis by overexpressing PCAF in the absence (or presence) of KMT2A, monitoring rRNA expression, and then plan to undertake future experiments accordingly.

(3) The catalytic-independent function of KMT2A should be directly investigated. The absence of a significant change in H3K4me3 levels following KMT2A depletion does not confirm that KMT2A's catalytic activity is not essential. Rescue experiments comparing wild-type KMT2A with a catalytically inactive variant would provide a much stronger assessment of the proposed non-catalytic mechanism.

We thank the reviewer for their comment. We completely agree that it is important to rule out whether catalytic activity of KMT2A is essential for rRNA transcription. We have shown in Fig. 4G that the catalytic point mutant carrying the N3906A mutation is able to recruit PCAF and RNA Pol I to the rDNA but not the KMT2A∆TAD mutant. This rescue experiment supports our hypothesis that the catalytic activity of KMT2A is not involved in mediating transcription at rDNA, but TA domain-dependent recruitment of PCAF is critical.

(4) The manuscript highlights H3K9ac; however, various acetyltransferases and histone acetylation marks are linked to active rDNA. The authors should investigate whether KMT2A specifically regulates H3K9ac or leads to broader changes in histone acetylation at rDNA.

We thank the reviewer for their comment. This is indeed an insightful suggestion. As shown in Fig 3. Multiple histone acetylation marks decorate the rDNA, and it is not possible for us to test them all. We propose to test some of these marks during revision to gain insight into the range of KMT2A-mediated regulation.

(5) Due to the highly repetitive nature of rDNA, the manuscript must include detailed information about the reference assembly, mapping strategy, management of multimapping reads, normalisation processes, and biological replicates. The authors should demonstrate that any observed changes in occupancy are not due to technical differences in rDNA mapping or variations in copy number.

We thank the reviewer for their comment. As indicated in the manuscript, we have used the pipeline from George et al. al, 2023, PMID: 37121547, which describes all these parameters in detail. Hence, we have omitted a repetition here but added a brief sentence in the Methods now.

(6) KMT2A regulates a wide range of transcriptional programs, and its depletion can affect proliferation, cell-cycle distribution, or nucleolar function. The authors should include appropriate controls to demonstrate that the rDNA phenotype is not a result of changes in cellular proliferation or a generalised response to transcriptional or nucleolar stress.

We thank the reviewer for highlighting this important point. The transcriptional profiling recently published by our lab [Lone et al. (2026), PMID: 42096476; Malik et al., 2023, PMID: 37379335] provides clear evidence that helps distinguish direct regulatory effects from generalized stress responses. Our global transcript analysis indicates that KMT2A depletion specifically downregulates transcription at the rDNA repeats without inducing hallmark markers of nucleolar stress or broad cell-cycle arrest.

(7) The CSB and B-WICH complex have previously been linked to the recruitment of PCAF and the acetylation of H3K9 at active rDNA. The authors should investigate whether KMT2A operates independently of these factors or if KMT2A functions within an established pathway for remodeling rDNA chromatin.

We agree with the Reviewer that CSB and the B-WICH complex, PCAF recruitment, and H3K9ac deposition are indeed a well-documented axis at active rDNA. In the present study, our focus is on establishing the functional role of KMT2A at the rDNA locus. Given that KMT2A traditionally acts as a histone methyltransferase that often precedes or cooperates with acetyltransferases like PCAF, it is highly plausible that KMT2A operates sequentially or in concert with the B-WICH pathway to remodel chromatin.

However, mapping these biochemical interactions is beyond our current aims. Nonetheless, we agree this is a crucial conceptual link, and we will expand this link in our Discussion.

(8) The distinction between active and silent rDNA should be taken into account. The authors need to determine whether KMT2A/PCAF occupancy is preferentially associated with active rDNA copies. Sequential ChIP analysis or the use of established markers for active, poised, and silent rDNA would help clarify the chromatin context in which the proposed mechanism operates.

We appreciate the Reviewer’s suggestion to determine if KMT2A/PCAF occupancy is restricted to active rDNA copies. While this is an important factor to consider, making a clear distinction is currently not possible due to several constraints. First, the highly repetitive nature of rDNA repeats makes it difficult to differentiate active from silent fractions both experimentally and bioinformatically. Second, performing sequential ChIP to definitively map this co-occupancy is technically challenging and establishing and optimising this protocol within the revision timeframe will be extremely difficult.

Furthermore, the exact histone landscapes defining active, poised, and silent rDNA are not yet fully characterized; much of the existing consensus in epigenetic literature relies heavily on observations drawn from RNA Polymerase II systems rather than Pol I repeats. As demonstrated by Xie et al., 2012 [PMID: 22570494], rDNA promoters frequently feature bivalent marks—bearing both active H3K4me3 and repressive H3K27me3 modifications—that characterize a poised, non-transcribing state. This biological ambiguity makes absolute active/silent categorization extremely difficult in our case.

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Author response:

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

eLife Assessment:

The study by Izquierdo and colleagues provides important insights into the field of genomic and transcriptomic prediction of traits across multiple environments. The rationale and analyses conducted to integrate the two types of ~omics datasets across two environments are solid. However, some clarification would be appreciated in the presentation of the results, and adding some statistical control to clarify how the predictors were selected, or assessing their importance using the SHAP framework, would further consolidate the findings.

We appreciate the positive feedback and the constructive evaluation of our work. In response, we have added further clarification to the Results section and provided additional detail on the feature selection procedure to facilitate understanding of how predictors were identified within the modeling framework.

Public Reviews:

Reviewer #1 (Public review):

Summary:

P. Izquierdo et al. investigated the genetic determinism of various traits of interest in switchgrass using large-scale genomic and transcriptomic data. More specifically, they worked on a diversity panel comprising 426 genotypes evaluated in common-garden experiments at two locations (Michigan and Texas). The phenotypic and genomic data were already published. In this work, they produced transcriptomic data for each of the 426 genotypes at each site, and they carried out phenotype predictions using genomic and transcriptomic data separately or together. While they were moderately correlated at each location, both omic information appeared to be complementary for the prediction of phenotype. To further exploit the fact that they have data across two locations, they computed differences for phenotypes and transcripts between locations as indicators of trait and transcript plasticity, respectively. They built predictive models of trait plasticity using genomic information and transcript plasticity, which proved to be quite accurate for traits affected by GxE. Finally, they made use of SHAP values from predictive models of flowering time and biomass at each location, as well as for their plasticity, to gain insight into their genetic determinism. These SHAP values provide the importance of the predictive features (SNP and/or transcripts) for trait prediction. This allowed them to confirm some candidate genes and to propose new candidates for both traits.

We appreciate the reviewer's thorough and constructive summary of our work. We would like to clarify that while the genomic data were previously published, the transcriptomic and phenotypic data were generated as part of the present study. We have revised the text to make this distinction explicit.

Strengths:

I found this study interesting and rich. I think the sample size (426 genotypes) is large enough to support the findings. The use of a modern machine-learning approach (XGBoost) together with SHAP indices to find interesting features and get insights into the biological mechanisms underlying flowering time and biomass production is quite original. The methodology employed is globally sound. I also like the fact that the authors accounted implicitly for the population structure by providing a baseline prediction using the first 5 PCs.

Weaknesses:

While the methodology is globally sound, I sometimes had difficulties following exactly what was done. This is partly due to the fact that the authors used 2 omics (SNPs and transcripts) to predict phenotypes, and sometimes, in the results, it is not clear which of the 2 is the focus. This was especially the case for the importance of the features and the interpretability of the models, where I found it sometimes hard to tell whether the analysis was done on SNPs or transcripts.

We have revised the text throughout to clarify when models using SNP, transcript (T), or both data types (S+T) were the focus of the analysis.

Also, regarding the methodology, I did not understand why the authors needed to perform a feature selection approach. Maybe it was required to perform the interaction analysis, which could not be deployed on all the features? But regarding the importance of the features, I do not get the added value of the selection over the direct use of SHAP indices when using all features. Maybe this is because I am not a specialist in this kind of approach, but maybe the authors could add more details to explain the rationale behind the feature selection.

Feature selection was performed to identify the subset of features that optimized predictive accuracy while reducing model complexity. By retaining only the most informative features, the resulting models achieve higher predictive accuracy than models trained on all features, and model interpretation is simplified. The rationale and procedure are described.

Regarding SHAP interactions specifically, the number of features used to estimate SHAP interaction scores was limited to 5,000 due to the high computational demands of this analysis. Interaction scores are estimated for each individual in the training population, producing a 5,000 × 5,000 interaction matrix per individual. With 306 individuals in the training population and 10 independent model runs, this corresponds to 3,060 matrices of this size.

Reviewer #2 (Public review):

Summary:

The authors aimed to evaluate whether integrating genomic (SNP) and transcriptomic information with machine learning can improve phenotypic prediction of polygenic traits across environments. The manuscript explored not only the predictability across models and predictor feature sets, but also attempted to identify meaningful genes and interactions underlying trait variation.

Strengths:

The main strength of the manuscript is its integration of SNP, transcriptomic, and phenotype datasets for 426 sorghum genotypes between Texas and Michigan. It provides a systematic comparison of predictor types (SNP versus transcriptomic abundance) and model strategies to integrate them.

Weaknesses:

(1) Experimental Design

The experimental design raises several concerns that should be clarified before strong biological conclusions are drawn from the transcriptomic analyses.

First, the transcriptomic sampling is not well aligned with the developmental stages most relevant to the phenotypes being modeled. Leaf tissue was collected at a single time point in each environment, whereas traits such as flowering time, biomass, tiller count, and panicle height arise from developmental processes occurring over extended and potentially distinct temporal windows. Consequently, the measured expression profiles are likely to reflect physiological states specific to the sampling dates (May 5-6 in Texas and June 22-24 in Michigan) rather than the regulatory processes underlying the target phenotypes.

We selected the pre-flowering stage because it represents a critical developmental transition during which plants remain largely vegetative while initiating reproductive development. Gene expression at this stage is therefore expected to capture regulatory processes associated with flowering initiation while also reflecting pathways involved in vegetative growth and biomass accumulation. In our previous work in maize (Azodi et al., 2020), we demonstrated that transcriptomic profiles obtained at a single developmental stage can contain information predictive of complex traits. Although the expression profiles analyzed here do not capture the full temporal dynamics underlying traits such as flowering time and biomass, they provide a biologically meaningful snapshot of molecular variation relevant to these traits. We have revised the manuscript to acknowledge this limitation and to clarify that our findings should be interpreted as associations between gene expression measured at the pre-flowering stage and the phenotypes of interest, rather than as evidence that all identified genes directly regulate these traits throughout development.

Second, the phrase "haphazardly randomized" is questionable for a field experiment. It is unclear whether the design included formal randomization, blocking, row/column structure, or spatial correction. Without explicit accounting for spatial field heterogeneity, environmental variation within sites may confound genotype and transcriptomic effects.

We thank the reviewer for this comment and agree that the original wording was unclear. The text has been revised to more precisely describe the experimental design. The establishment and management of the common gardens are described in detail in Lovell et al. (2021). Briefly, the diversity panel was established as a single-block planting at each location, with genotypes distributed throughout the field and arranged in a honeycomb design in which each individual had four nearest neighbors located 1.5 m apart. We have removed the phrase "haphazardly randomized," which was imprecise.

Because only a single replicate of each genotype was established at each site, formal spatial correction was not performed, as genotype and within-site spatial effects cannot be estimated independently in this design. We acknowledge that additional replication would have improved our ability to account for fine-scale environmental heterogeneity.

However, several aspects of the experimental design reduce the likelihood that spatial variation substantially confounded the results. The diversity panel is part of a coordinated common garden network spanning ten field sites across the United States, designed primarily to evaluate genotype-by-environment interactions across contrasting environments rather than within-site spatial variation. In addition, the AP13 reference genotype was distributed throughout the experimental plots and did not show evidence of substantial spatial heterogeneity at the Michigan site, suggesting that within-site environmental variation was limited. We have added text acknowledging this limitation and its implications for interpreting genotype and genotype-by-environment effects.

Third, the Methods do not clearly describe biological replication for RNA-seq. If each genotype-by-environment combination were represented by a single transcriptomic sample, then within-genotype expression variance cannot be estimated. This is important because transcript abundance is highly sensitive to microenvironment, sampling time, tissue status, developmental stage, and technical variation. The absence of replication significantly weakens confidence in gene-level feature importance and gene-gene interaction claims.

We appreciate this thoughtful comment and fully acknowledge that the absence of biological replication for RNA-seq within each genotype-by-environment combination is an important limitation of this study. Because the diversity panel consisted of a single plant per genotype at each field site, transcriptomic data were generated from one biological sample per genotype-by-environment combination, and within-genotype expression variance could not be directly estimated. We recognize that transcript abundance can be influenced by microenvironmental conditions, developmental stage, tissue status, sampling time, and technical variation, all of which may affect confidence in gene-level feature importance and inferred interaction effects.

The scale of the experiment, involving 426 genotypes evaluated across contrasting common gardens, made biological replication for RNA-seq financially and logistically impractical. This experimental design was established to maximize representation of genetic diversity and environmental variation across a large multi-environment common garden network rather than to obtain replicated transcriptomic measurements within individual sites. To minimize uncontrolled variation, tissue was collected at both locations at approximately the same pre-flowering developmental stage, and standardized protocols for tissue collection, library preparation, sequencing, and data processing were applied across all samples.

Although individual genotype-by-environment combinations were not biologically replicated, the analyses leverage substantial replication at the level of alleles and population structure, as individual alleles and transcripts are represented across many genetically distinct accessions spanning multiple ecotypes. This is analogous to many human population-scale transcriptomic studies, where each genotype is typically represented by a single biological sample and inference is made across genetically diverse individuals rather than replicated measurements of the same genotype.

Importantly, the goal of this study was to identify transcriptomic patterns that are predictive of phenotypic variation across genotypes and environments, rather than to establish causal regulatory relationships. Accordingly, the genes and interaction patterns identified through model interpretation should be viewed as candidate predictive associations and hypothesis-generating signals that warrant validation in future studies with replicated sampling and controlled experiments. We have revised the manuscript to more clearly acknowledge these limitations and to align the interpretation of gene importance and interaction analyses with the predictive scope of the study. 

Four, the analysis of expression differences across environments is based on a simple subtraction (TX - MI) followed by correlation with genetic similarity. This approach is not standard in transcriptomic analysis and does not account for variability, replication, or statistical uncertainty. Conventional methods for assessing differential expression and genotype-by-environment interactions rely on model-based frameworks that explicitly estimate variance components and test for interaction effects. Without such modeling, the observed expression differences may reflect noise or confounding factors rather than genotype-driven responses.

We appreciate this comment. Our approach to estimating expression differences across environments was intended to quantify transcriptomic plasticity and evaluate whether variation in gene expression responses across environments could help explain and predict phenotypic plasticity. While this is not a conventional differential expression framework, our objective was not to identify differentially expressed genes or formally test genotype-by-environment interaction effects at the transcript level.

Expression differences were calculated as TX − MI using log-transformed expression values. On the logarithmic scale, this difference is equivalent to the log expression ratio between environments and therefore provides a straightforward measure of the magnitude and direction of transcriptomic responses across locations. We used this metric as a descriptive measure of transcriptomic plasticity that could be related to genetic similarity and incorporated into predictive models of phenotypic plasticity. Consistent with this rationale, models based on expression differences across environments were able to predict differences in phenotypic performance between locations.

(2) SHAP contribution values

Although SHAP is a well-established framework for decomposing model predictions into feature-level contributions, its use in this manuscript raises several concerns regarding interpretation, statistical validity, and biological inference.

First, SHAP values quantify the contribution of features within the fitted model, conditional on the joint distribution of inputs and the model structure. They do not represent causal effects or direct biological importance. 

We agree that SHAP values do not represent causal effects or direct measures of biological importance. Rather, SHAP quantifies the contribution of features to model predictions within the context of a fitted model and the observed input distribution. Our rationale for using SHAP was not to infer causality, but to identify features that are consistently informative for predicting phenotypic variation. The underlying hypothesis is that features contributing strongly to accurate predictions may be associated with biological processes influencing the trait and can therefore serve as candidate genes or genomic regions for further investigation. This strategy has been widely adopted in genomics and plant biology, where interpretable machine learning methods are used to extract biological insights from predictive models. Accordingly, the genes and interactions highlighted by SHAP should be interpreted as predictive associations and candidate mechanisms requiring validation through independent experiments and functional studies. We have revised the manuscript to more clearly distinguish predictive importance from causal biological effects.

There is a difference where SHAP values are often in log-odds and the regression model uses absolute units. 

We thank the reviewer for this comment. We believe there may be a misunderstanding regarding the scale of the SHAP values reported in this study. The models analyzed here are regression models predicting continuous traits, not classification models. Consequently, SHAP values are expressed in the same units as the predicted phenotype and represent the additive contribution of each feature to individual predictions. The interpretation of SHAP values in log-odds units is specific to certain classification models where predictions are generated on the log-odds scale. We have revised the manuscript to clarify this point and avoid potential confusion.

Without a fair evaluation of model fit, the interpretation of SHAP values needs to take a cautious step because a model could fit poorly when a feature shows very high SHAP values.

We agree that SHAP values should be interpreted in the context of model performance. For this reason, model performance was evaluated prior to feature interpretation. Figure 1 presents the predictive performance of all models, and we focused our biological interpretation on flowering time and biomass because these traits are agronomically important and showed relatively stronger predictive performance compared to other traits, providing a more reliable basis for interpreting feature importance. We have revised the manuscript to emphasize that model interpretation should be considered in conjunction with model accuracy.

In genomic data, where features are highly correlated due to linkage disequilibrium and co-expression, SHAP values can distribute contribution values across correlated variables in ways that are not uniquely identifiable. As a result, features highlighted as "important" may reflect correlation structure rather than true functional relevance.

We agree that multicollinearity can complicate the interpretation of feature importance, as correlated features may share predictive information, resulting in importance being distributed among them or assigned preferentially to one feature over another. This issue is particularly relevant in genomic datasets due to linkage disequilibrium among SNPs and co-expression among genes. To reduce redundancy among genetic markers, SNPs were filtered using a linkage disequilibrium threshold of r² < 0.1 prior to model training, substantially reducing the number of highly correlated markers. We acknowledge, however, that correlation among features, particularly among co-expressed genes, remains present and may influence SHAP-based feature attribution. 

To improve the robustness of feature interpretation, models were trained across 10 independent runs and SHAP values were averaged across runs, reducing sensitivity to individual model fits and providing more stable estimates of feature contributions. Nevertheless, SHAP values should not be interpreted as uniquely identifying the most functionally relevant feature within a correlated group of predictors. The genes and genetic variants highlighted by SHAP should therefore be viewed as candidate predictive features associated with trait variation rather than definitive evidence of causal biological relevance.

This correlative structure can be exacerbated in this manuscript because of the use of TPM-normalized transcript abundances as predictor variables without biological replicates. Assume the estimates of transcript abundances are robust, TPM values are compositional, with a constant-sum constraint that creates dependencies among all genes that induce negative correlations. This issue is particularly relevant for the interpretation of gene importance and interaction effects, where correlated predictors can lead to unstable and non-unique attributions. This biological interpretation of transcript-based features remains uncertain.

We agree that TPM-normalized expression values are compositional and may introduce dependencies among genes due to the constant-sum constraint. TPM normalization was selected because it facilitates comparisons of transcript abundance across samples by accounting for differences in sequencing depth and transcript length. Expression values were further transformed using log₁₀(TPM + 1), which reduces skewness and stabilizes variance, making the data more suitable for machine learning analyses. We acknowledge that compositional effects and gene co-expression may influence feature attribution and the interpretation of gene importance. However, the primary objective of this study was predictive rather than inferential. In this context, log-transformed TPM values provide a standardized and comparable representation of transcript abundance across genotypes and environments, serving as consistent input for predictive models. Consequently, genes identified through SHAP analyses should be interpreted as candidate predictive features associated with trait variation, rather than as definitive evidence of direct causal biological importance.

(3) Result interpretation

For example, in page 11, "plasticity SNP- and transcriptomic-based models generally outperformed single-environment models for traits with low cross-environment correlation, such as green-up (Fig. 2c, r = -0.13, p < 8.3 × 10^-3) and tiller count (Fig. 2f, r = -0.08, p = 0.1) (Supplementary Fig. S1)." is too broad. For green-up, the Diff model appears much better than MI, but not clearly better than TX.

We thank the reviewer for this observation and agree that the original wording was too broad. We have revised the text to more accurately reflect the observed pattern, noting that difference-based models showed relatively stronger predictive performance for traits with low cross-environment correlation, while generally performing worse than single-environment models for traits with high cross-environment correlation. We believe this pattern is biologically meaningful, as transcriptomic differences across environments are expected to be most informative when phenotypic responses differ substantially between locations. We have revised to more accurately characterize these results.

And, same page 11, "...Diffexp was more predictive than SNPs for trait plasticity in biomass, flowering time, and tiller count..." only holds true for biomass, not flowering time, or tiller count.

We thank the reviewer for this observation and agree that the original statement was too strong. Diffexp models showed higher predictive performance for biomass and tiller count, whereas performance for flowering time was comparable between Diffexp and SNP models. We have revised to more accurately characterize these results.

The aspect of "complementary information" between SNP and transcriptomic models in page 12 is stronger than what is supported by Figure 2. Figure 2 shows different predictive performance, but it does not by itself demonstrate complementarity. Establishing complementarity requires evidence that combining SNP+T improves prediction consistently or captures distinct, non-overlapping signals. Yet the preceding section says SNP+T outperformed either single data type in only 15% of cases, with modest gains. This is confusing. Also, there was not G+T in Figure 2; it is SNP+T.

We agree that the term "complementary" was stronger than what the results in Figure 2 directly support. We have revised the text to describe these findings more cautiously, emphasizing that SNP and transcriptomic models may capture partially distinct aspects of biological variation. In the following section, we further address this point by showing that the two model types identify largely distinct sets of predictive features, suggesting that they reflect different sources of information relevant to trait prediction. We also thank the reviewer for noting the SNP+T vs. G+T inconsistency, which has been corrected throughout the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I found that the title does not properly reflect the content of the paper. The term "artificial intelligence" is a bit misleading: I was expecting deep learning-based predictions. GxE and plasticity are clear strengths of the paper that are not present at all in the title. The same holds for multi-omic integration. Maybe you could consider revisiting the title.

We thank the reviewer for this suggestion and have revised the title to: "Multiomic integration using interpretable machine learning reveals genetic mechanisms of trait variation and phenotypic plasticity in switchgrass." This revision highlights the integration of genomic and transcriptomic data, explicitly mentions phenotypic plasticity, and replaces "artificial intelligence" with "interpretable machine learning," which more accurately describes the modeling framework employed.

(2) In general, the quality of the figures is very poor, and it did not allow me to perform a deep assessment of their content, which is sometimes hardly visible.

We agree that figure quality in the submitted PDF was suboptimal. The reduction in image resolution occurred during conversion from the original Word document to PDF. We have uploaded a revised manuscript with higher-resolution figures to ensure all elements are clearly visible.

(3) To estimate plasticity in phenotypes and transcripts, you use differences between locations. Other options have been proposed in the literature, like ratios, for example. I think the choice of the difference is probably a good one, but maybe you could justify it in the introduction.

We chose to estimate phenotypic and transcriptomic plasticity using differences between locations because this metric preserves both the magnitude and direction of environmental responses while avoiding the instability associated with ratio-based measures, particularly when values are small. Furthermore, because transcript abundance values were modeled using log₁₀(TPM + 1)-transformed data, differences between environments are conceptually equivalent to log expression ratios, as log(A) − log(B) = log(A/B). This justification has been added to the manuscript.

(4) Figure 1. I wonder why you computed correlation matrices between genotypes for transcriptomic data instead of simply covariance matrices, which would be closer to the genomic relationship matrix.

Our intention in Figure 1 was to visualize overall similarity among samples based on transcriptomic expression profiles across genes. We used Pearson correlation because it is widely applied in transcriptomic analyses to capture relative expression patterns while remaining independent of absolute expression magnitude and scale differences among samples. Covariance matrices, by contrast, are strongly influenced by feature variance and scale, which can complicate interpretation of overall transcriptomic similarity in high-dimensional expression datasets.

(5) Figure 1. You calculate correlations between phenotypic distance and genomic distances for the different traits, but I think this is somehow related to the genomic heritability estimation. Could you please elaborate on this or provide the rationale under your analysis?

We agree that the correlation between genomic relationships and phenotypic similarity is conceptually related to genomic heritability, as both analyses evaluate the extent to which genetic similarity is associated with phenotypic variation. However, their objectives differ. The correlation analysis between SNP, eCor, and phenotypic distance was intended as an exploratory assessment of whether genetically or transcriptomically similar genotypes tend to exhibit similar phenotypic responses across traits and environments. Genomic heritability estimation, in contrast, provides a formal variance component framework to quantify the proportion of phenotypic variance explained by genome-wide marker information. While related conceptually, these analyses address complementary but distinct aspects of the relationship between genomic, transcriptomic, and phenotypic variation.

(6) L163-164: "Because genotypes with similar genetic information are expected to exhibit similar trait value": this is the definition of the heritability, so I would say that this is true to the extent of the heritability of the trait... Maybe you could consider modifying this sentence.

Thank you for this suggestion. Our intention was not to invoke heritability directly, but rather to assess the associations among kinship, eCor, and phenotypic similarity within each environment and to compare the patterns captured by these different data types. We agree that the original wording could be interpreted as implying a deterministic relationship between genetic similarity and phenotypic resemblance. We have revised the text to focus on the association between genetic relatedness and similarity in expression and phenotypic profiles.

(7) Figure 2. For the prediction with transcriptomic data, I understood that you matched data by site for the prediction, which is OK. But I wonder what would happen if you had used transcriptomic data from the other site and vice versa for the prediction, how much predictability you would have lost? I guess that this would somehow be related to the extent of GxE for each trait. Maybe it would be something interesting to look at?

We thank the reviewer for this thoughtful suggestion. While cross-environment prediction is an interesting avenue for future research, our primary objective was not to maximize prediction across environments, as predictive ability would be expected to decrease substantially under strong G×E effects. Instead, we focused on single-environment models to: (1) identify transcriptomic features associated with trait prediction within each environment, and (2) evaluate which features were consistently important across environments. Furthermore, because G×E effects were observed, we developed TX − MI difference models to identify transcriptomic features associated with phenotypic plasticity. We therefore believe that the within-environment and plasticity-focused analyses were more closely aligned with the objectives of this study than cross-environment prediction would have been.

(8) The calculation of local SHAP values for each genotype mentioned L331 and the clustering of genotypes based on such values, as presented in Figure 4, are not presented in the method section. Could you please provide more details?

The estimation of SHAP values is described in the Methods section. Briefly, local SHAP values were calculated for each genotype, and genotypes were subsequently clustered based on these values using hierarchical clustering with Euclidean distance.

(9) Gene-by-gene interactions paragraph: I am a bit confused here regarding which omic was used for looking at the interaction. Naively, I would have gone with the SNPs, but maybe you would rather use the transcripts instead? This would explain why in Figure 5 c-h, the x axes seemed to correspond to transcripts rather than SNPs. Could you please clarify and explain why you focused here on transcripts rather than SNPs?

We thank the reviewer for this comment. To clarify, gene–gene interactions were assessed using transcriptomic models. This choice was motivated by three observations: (1) transcriptomic features were enriched among the most important predictors in the multi-omic models; (2) transcriptomic models identified a greater number of benchmark genes than SNP-based models; and (3) gene expression data provide a more biologically interpretable framework for assessing gene–gene interactions, as transcripts more directly reflect gene activity and regulatory processes than individual genetic variants. We have revised the manuscript to make this rationale explicit.

(10) Materials and Methods:

- Were there replicates of the genotypes within each site?

This diversity panel is part of a multi-institutional project maintaining 10 common gardens across the United States. Given the scale of the experiment and the large number of genotypes evaluated, the design included a single plant per genotype at each site rather than within-site replication. We acknowledge this as a limitation and have discussed it explicitly in the revised manuscript.

- Have the data (phenotypic/transcriptomic) been corrected for spatial effects?

Because only a single replicate per genotype was evaluated at each site, genotype and local spatial effects could not be estimated independently. Applying a spatial correction under these conditions could inadvertently remove true biological variation. The randomized honeycomb design was intended to minimize systematic spatial confounding; however, we acknowledge that residual environmental heterogeneity may still contribute to phenotypic and transcriptomic variation.

- L502-503: Could you please write the model formally instead of R code?

The model has been written formally.

- Genomic heritability estimates: I wonder how useful they really are? I suppose you could have used the model L502-503 to estimate genomic heritability in general across the 2 sites.

We agree that the mixed model described in the revised manuscript could be used to estimate genomic heritability jointly across both sites. In this study, however, genomic heritability was estimated within individual environments to evaluate trait predictability within each location and to assess the heritable component of phenotypic plasticity. Genomic heritability also provides an important benchmark for interpreting prediction results, as the theoretical upper limit of prediction accuracy is approximately proportional to the square root of heritability under quantitative genetic theory.

- L523: I am not sure what LD> 0.1 means. Could you please give more details, e.g., which measure of LD, which software, and which parameters?

We have clarified this point in the Methods. LD pruning was performed using the +prune plugin in BCFtools, with pairwise LD measured as the squared Pearson correlation coefficient (r²). SNPs with r² > 0.1 within a 5 Mb sliding window were removed to retain a set of more independent markers.

- L526: How many leaves were sampled per plant? Or maybe a particular leaf was chosen?

For each plant, we collected the fully expanded leaves at the highest point on each tiller. The proximal ~4 cm (length of microcentrifuge tube) of that harvested leaf was then flash-frozen in liquid nitrogen for subsequent RNA extractions.

- L592-597: I understand that training and test sets were stratified according to biomass (log-transformed) in TX. Could you please explain why this trait/location was chosen for the stratification?

Training/test stratification: We chose log-transformed biomass in TX for stratification because biomass is the primary agronomic trait of interest in switchgrass and exhibits greater phenotypic variation in TX compared to MI, allowing stratification to better preserve the full range of values in both the training and testing sets. The same training/testing split was subsequently applied to all analyses to ensure consistent and fair comparisons across traits, environments, and data types.

(11) Data availability: Maybe the read counts could also be provided on top of the raw RNA sequences. This would ensure, to some extent, reproducibility of the analyses, especially because the code for processing RNA-seq reads does not seem to be released in the GitHub repository.

The RNA-seq pipeline used in this study is described in the revised manuscript. The pipeline code is maintained in an internal GitLab repository at JGI and is therefore only accessible within JGI systems. To facilitate reproducibility, we have deposited the TPM count matrix used in our analyses in the following Zenodo repository: https://zenodo.org/records/21781035

(12) Code availability: The code to run Bayesian regression models does not seem to be released.

The code for the Bayesian regression models has been added to the manuscript repository.

Reviewer #2 (Recommendations for the authors):

The manuscript will benefit the most from additional biological replicates for RNAseq, as well as the phenology alignment with data collection. Further recommendations for improving the clarity in experimental design and alignment between claims and evidence.

We agree that additional biological replication for RNA-seq and transcriptomic sampling across multiple developmental stages would further strengthen the study. However, given the scale of the experiment, 426 genotypes evaluated across contrasting field environments, generating replicated transcriptomic datasets at multiple developmental stages was not logistically or financially feasible. Despite these constraints, the experimental design enabled characterization of transcriptomic and phenotypic variation across a large natural diversity panel and the identification of predictive patterns associated with trait variation across environments. We have revised the manuscript to more clearly describe the experimental design, sampling strategy, and study limitations, and to ensure that conclusions are appropriately aligned with the evidence presented.

Minor corrections:

(1) MAF threshold in Line 522, page 27. It should be > 0.05?

Corrected to > 0.05. 

(2) SNP+T versus G+T.

Revised to SNP+T consistently throughout the manuscript. 

(3) Include FDR-adjusted p-value thresholds.

FDR-adjusted p-value thresholds: For the Pearson correlations reported in this study, each represents a single pre-specified comparison rather than a family of simultaneous tests, and raw p-values are therefore appropriate. For the benchmark gene enrichment and Wilcoxon rank-sum tests, where multiple comparisons were performed across models and traits, FDR correction has been applied using the Benjamini– Hochberg procedure and the reported p-values have been updated accordingly. 

(4) Avoid ambiguous phrasing like "generally consistent" and "generally outperformed".

Revised throughout the manuscript. 

(5) The mention of artificial intelligence in the Abstract is largely conceptual and reads more like discussion material rather than the main finding of the manuscript, per eLife's Abstract requirements.

The mention of artificial intelligence has been revised in the Abstract in accordance with eLife's guidelines.

Author response:

We thank the reviewers for their careful evaluation of our manuscript and their constructive feedback. We appreciate the points raised and will take them into consideration when revising the manuscript.

We plan to clarify and refine certain aspects of the interpretation and discussion, particularly regarding the relationship between Samp1, chromatin organization, and myogenic differentiation. We will also aim to strengthen the study with additional experiments and analyses where feasible, addressing the reviewers’ suggestions to the extent possible within the scope of the study.

We believe these revisions will help improve the clarity and strength of the manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, the authors study the migration of isolated cells and of cells in ensembles. They quantify several aspects of the corresponding migration patterns and investigate how these quantities depend on molecules that are known to play an important role in migration. Furthermore, they study the effect of external cues on these migration processes.

Strengths:

The authors provide a clean and uniform setting for comparing the migration of isolated cells and of cells in an ensemble in control and mutant conditions, and in the presence and absence of external cues. This allows for a meaningful comparison between different conditions. In this way, the authors obtain useful data that link the migration of isolated cells to that of cells in collectives.

Weaknesses:

A major weakness of the manuscript is that the authors do not properly introduce the quantities and concepts they are working with. In this way, it is hardly accessible for a reader who does not have a thorough background in cell migration and anomalous transport. In addition, the manuscript uses some notions that are not standard, for example, vinculin or FA stability, which are not properly introduced. Most strikingly, "collective directional memory" is not defined.

We thank the reviewer for pointing this out. We have now added the definition of collective directional memory in the introduction:

“... cells that migrate collectively acquire long-term directional memory, which specifically requires α-catenin in AJs and results from coordination of velocities between neighboring cells. For this reason, we define it as a collective directional memory.” and in the results section:

“... the transition in directional memory observed at confluence are the results of bona fide AJ-mediated intercellular adhesion, but independently of the cadherin subtype. Consequently, we define as a collective directional memory this long-term directional memory that arises from neighbor interactions.”

The definition of anomalous transport is given in the results section too:

“we found that the average Mean Square Displacement as function of lag time ∆t (MSD, see Materials and Methods) was better described by a persistent random walk (Fürth et al. 1920, Uhlenbeck et al. 1930) than anomalous diffusion: the MSD transitioned from ballistic (MSD ∼ ∆t²,∆t → 0) to pure diffusion (MSD ∼ ∆t,∆t → ∞) with a persistence time P of the order of 10min, rather than scaling as ∆t^𝛼 with α ̸\= 1” and in the Materials and Methods:

"MSD(∆t) curves were fit with the Fürth equation MSD = 4_D_(∆t−P(1_−exp(−∆_t/P))) where D is the coefficient of diffusion and P the persistence time, as a model of persistent random walk, or with MSD ∼ ∆t^𝛼 (straight line of slope α in ln−ln scale), as a model of anomalous diffusion, with anomalous exponent α > 1 for super-diffusion."

The definition of vinculin and FA stability, which we now specify as “molecular stability” is given in the Materials and Methods section:

“We use the immobile fraction of vinculin and its mutants as a measure of vinculin stability and, by extension of the molecular stability of adhesions, because the stability of other adhesion proteins is regulated by the stability of vinculin (Carisey et al. 2013, Liu et al. 2016, Yonemura et al. 2010).”

The authors infer relationships between different quantities, but they remain qualitative, even though the authors use a language that suggests otherwise. For example, "The combination of Focal Adhesion stability and force transmission from the cytoskeleton predicts the migration speed of single cells" (p 2). I am not sure what is meant by prediction, but this heading suggests that knowledge of FA stability and force transmission yields the migration speed. Reading this line, I expect that if I give you values for FA stability and force transmission, you would give me a value for the migration speed. Such a quantitative mapping is not provided. In fact, it cannot be provided, because - as mentioned before - these quantities are not properly defined, so I would not know how to measure them. I do not even know their units.

We thank the reviewer for suggesting a more quantitative analysis. Initially, we used Boolean logic to build our model. Based on the effects of mutants, vinculin can be either tensed or not, and either stable or not, which yields four combinations that associate with more or less fast migration. We represent the model as a Venn diagram, which we now specify in the results section and figure legends. To complement this simplified approach, we have now added quantitative analyses by fitting changes in single cell speed, in the difference between single and collective cell migration speed, and in the ratio between collective cell migration speed and wound healing rate to the changes in tension, stability, or the gradients of tensions in FAs and AJs based on the quantitative measurements of speed (migration assays), tension (FRET index of vinculin sensors) and stability (immobile fraction of FRAP experiments) re-scaled between their extreme values across vinculin constructs, as explained in the Materials and Methods. This allows us to quantify the contributions of changes in tension, stability, and the gradients of tension to changes in single cell migration speed, in the difference between single and collective cell migration speed, and in the ratio between collective cell migration speed and wound healing rate. As shown in the added Fig. S2I, the change in single cell speed is explained by a linear combination of changes in tension and stability with contributions of 2_/3 and 1/_3, respectively. In Fig. S4J, the difference between single and collective cell migration speed changes with the stability exclusively, and its increased sensitivity to low stability is well captured by a power law. In fig. S5C, the ratio between collective cell migration speed and wound healing rate is set by the difference in mechanosensitivity between FAs and AJs in which 1/3 of that of AJs counts. Overall, these results confirm our initial models.

Furthermore, the authors do interpret some of their results without explaining or justifying the basis for their interpretation. For example, they use the FRET index of vinculin - another notion that is not properly introduced - to make statements about mechanical stress.

We are sorry that we had overlooked this important explanation. We have now added explanations in the main text, and in the Materials and Methods. Briefly, the FRET sensor module inserted in vinculin and its mutants is made of two fluorescent proteins separated by an elastic polypeptidic linker of known elasticity, such that an increase in tension on the protein will stretch the sensor and will decrease the amount of FRET between the two flanking fluorescent proteins. As a result, the lower the FRET, the higher the tension. We cite the original paper that introduced this sensor to allow the reader to get more information (Grashoff et al. 2010). Figures now also include the direction along which the tension increases when FRET changes.

It also seems that the figures could be improved. Some of the sketches are, in my opinion, not helpful. Examples are Figure 3A (how could a cell move while the hexagonal arrangement of the cells is maintained?) or Figures 2F, 4F, and 6F (what do the colored ellipses indicate?). In Figures 1B, 1D, 2A, 2E, 3B, 3D-F, 4A, 4F, 5B-D, it is not clear which lines merely connect data points and which lines are fits to the data.

We thank the reviewer for suggesting these improvements. We have now changed figure 3A for a more realistic drawing of the epithelium. We have specified in figure legends what colored ellipses are (as explained above, they are the Venn diagram categories), and whenever a line was a fit or a curve connecting data points.

Reviewer #2 (Public review):

Summary:

The manuscript by Canever et al was assessed by three Referees at another journal, who brought up a range of critical points. I will not repeat a summary of the work; this can be found in the first-round reviews.

Strengths:

In their revised manuscript, the authors include substantial changes and additional reasoning. Along with their rebuttal letter, I think they make a very convincing case. While the claims are well supported by the analysis, I do not see that the findings need to be universal to be relevant. It might be rather surprising to me if there existed such a universality, in fact. I think that the findings are solid and interesting in their own right and are worthy of publication, especially with the amended discussion in this revision.

Weaknesses:

However, while the more bio-oriented parts are not fully accessible to me, I do have a few points from the data analysis point of view that need amendment. (1) The used mathematical models need to be specified more precisely. First, the authors confuse Levy flights and walks. These are distinct processes in the sense that a Levy flight does not have a finite variance and thus no finite speed. The proper model here would be Levy walks. As in a big body of the literature, both notions are used interchangeably here, while they are distinct processes. Then the authors speak about a "superdiffusive model", for which I do not find a proper definition. There exists an entire range of superdiffusive models, each with a different physical background, so this needs more clarity. The authors may consult one of the standard reviews for more details, e.g., Soft Matter 8, 9043 (2012) or Phys Chem Chem Phys 16, 24128 (2014). Overall, a few equations (maybe in the Supplement) would help to be more specific.

We thank the reviewer for these suggestions. We have changed the main text as follows to address these points:

- "To distinguish between the various walk models that could produce such a super-diffusive behavior (Lévy walk, fractional Brownian motion, or their combinations."

- "we found that the average Mean Square Displacement as function of lag time ∆t (MSD, see Materials and Methods) was better described by a persistent random walk (Fürth et al. 1920, Uhlenbeck et al. 1930) than anomalous diffusion: the MSD transitioned from ballistic (MSD ∼ ∆t²,∆t → 0) to pure diffusion (MSD ∼ ∆t,∆t → ∞) with a persistence time P of the order of 10min, rather than scaling as ∆t^𝛼 with α ̸\= 1" and the Materials and Methods as follows:

- "MSD(∆t) curves were fit with the Fürth equation MSD = 4D(∆t−P(1−exp−∆t/P)) where D is the coefficient of diffusion and P the persistence time, as a model of persistent random walk, or with MSD ∼ ∆t^𝛼 (straight line of slope α in ln−ln scale), as a model of anomalous diffusion, with anomalous exponent α > 1 for super-diffusion."

We thank the reviewer for the additional references, we cite the more recent Meroz et al., 2015 for reference on anomalous diffusion.

(2) For fractional Brownian motion, the authors should check the displacement correlation function; it should show slowly decaying, positive correlations. More details on the practical analysis of FBM can be found, e.g., in Phys Chem Chem Phys 27, 14350 (2025). These correlations should decay as a function of the bin time, e.g., as discussed for the opposite case of subdiffusion in Phys Rev E 88, 010101(R) (2013) [cf Fig 3b]. In general, FBM was determined to be a highly relevant process for a number of systems, including amoeba cells at shorter times, see the detailed analysis in Phys Rev Res 4, 033055 (2022). In this paper, there are also different ways to characterise the motion in terms of scaling. Exponents are detailed.

We thank the reviewer for these suggestions and references. We have added explanations in the main text and in the Materials and Methods about the metric we use to characterize fractional Brownian motion together with the suggested reference Phys Chem Chem Phys 27, 14350 (2025).

In summary, we define the angular memory as a modified angular correlation in which we consider the angular deviation θ of each elementary step of duration 10min from its immediate previous step of duration τ equal to the lag time ∆t. Specifically, the angular memory _i,t(∆t) of a cell i at time t is defined as the cosine of the angle θ_i,t between consecutive step vectors between times t−∆t and t, and between times t and t+10min, such that the step duration τ of the first vector and the lag time ∆t before the next are equal. M_i,t(∆t) = cosθ_i,t (∆t) = cos . Figures display ⟨M_i,t(∆t)⟩. This metric measures the duration of the past that the cell considers when deciding on its direction. It decays to 0 when ∆t → ∞ for persistent random walkers and remains constant for fractional Brownian motion, similarly to the auto-covariance function of fractional Brownian motion C(∆t/τ) = ((∆t/τ +1)^α +|∆t/τ −1|^α −2(∆t/τ) ^α)/2, which is a constant C = 2^α-1 −_1 for all ∆_t \= τ, as in our definition of angular memory (while it decays to 0 when ∆t/τ → ∞, as pointed out by the reviewer) (Metzler et al. 2025). Ballistic motion yields 1 whatever ∆t and uncorrelated random walks, whether anomalous or not, yield 0. For this reason, and also because M_i,t(∆t) was found more robust to noise than C(∆t/τ), we considered this metric a more compelling discriminant between fractional Brownian motion and other uncorrelated super-diffusive walks.

(Of Note, we have increased the analysed data set in the revised Fig. 1D, 3D,F for the sake of representativeness. The conclusions are unchanged).

(3) Some relevant approaches discussed in literature that should be discussed in the context of this work: eLife 9, e52224 (2020); Rep Prog Phys 86, 126601 (2023); Chaos 35, 023145 (2025). In the context of non-Gaussianity for active particles: Phys Rev E 104, 064615 (2021); New J Phys 25, 013010 (2023).

We thank the reviewer for these interesting references. We have added them in the discussion as follows: "More recently, efforts have focused on developing analysis tools and models to account for heterogeneous migration properties along individual trajectories and among populations (Lemaitre et al. 2023, Khadem et al. 2021, Woszczek et al. 2025, Waigh et al. 2025, Han et al. 2020)." We have also made changes in the main text to specify when and how our data could indicate the presence or the absence of such heterogeneity in the migration of single cells and at confluence.

(4) In the abstract, I am having some issues with the formulation in the sentence: "This directional memory emerges from fractional Brownian motion". It sounds as if FBM were a fully clarified phenomenon. I would prefer some statement along the lines that the data are consistent with such a mathematical modelling approach.

We thank the reviewer for this suggestion. We have changed the formulation to "This behavior is consistent with a fractional Brownian motion that emerges from velocity coordination between neighboring cells with intact intercellular adhesion." After fixing these points, I think the manuscript will clearly warrant being shared.

Reviewer #3 (Public review):

This manuscript focuses on the presence/origin of directional memory during epithelial cell migration. It starts by analyzing single cells and then moves to more complex systems (confluent layers and scratch assays). The paper first demonstrates that the migration in all of these systems is well-described by persistent random walks, which likely emerge from fractional Brownian motion. This is an important demonstration, as it implies orientation memory in the systems. Then the paper proceeds to attempt to discern the origin of this memory and claims to establish key roles for adherens junctions and vinculin dimerization. While for the most part the manuscript is well-written, there are some significant overinterpretations in experimental results. The largest issue is demonstrating the role of vinculin dimerization, which is not a well-studied phenomenon inside living cells, as all data is reliant on a single point mutation (Y1065E). Additionally, the authors seem to be over-interpreting several of the assays; the statistical analysis does not seem to encompass all comparisons made, and the molecular model proposed does not clearly explain the observed results. The discussion could also be strengthened by considering other aspects of vinculin behavior (e.g., vinculin catch bonding) as well as discussing some other recent similar papers.

(1) Likely the most significant issue with the manuscript is the interpretation of the vinculin Y1065E variant and the assumption that the only defect the mutations cause is a lack of dimerization. Vinculin dimerization is mediated by a conformational change in the vinculin tail domain induced by F-actin binding (Thompson, FEBS Letters, 2013). Dimerization of the vinculin tail domain has been clearly demonstrated in in vitro systems involving purified proteins, as the authors point out in the manuscript. However, the dimerization of full-length vinculin has not been well characterised in living cells. There are several reasons to suspect dimerization is potentially not prevalent in cells. For instance, in the presence of other actin-binding proteins, there may not be sufficient binding sites available on neighboring actin filaments to facilitate dimerization. Additionally, pY1065 vinculin and vinculin Y1065E have been associated with increased vinculin activation (Huang, JBC, 2014), so other effects seem possible. While the Y1065E variant clearly has an effect on the tension sensor readout and vinculin dynamics, further experimental evidence is needed to show that these effects are due to a lack of dimerization in living cells. To justify the definitive claims made in the manuscript, the authors likely need to develop, or employ, an assay for detecting vinculin dimerization in living cells. The authors could choose between intermolecular FRET, proximity labeling assays (i.e., antibodies with DNA for signal amplification), bimolecular fluorescent complementation (i.e., split GFP) based approaches, or some other approach. It should be noted that working with full-length vinculin, not just Vt, and designing an assay that can incorporate vinculin Y1065 variants (Y1065E and potentially Y1065A/F) would strengthen results. Also, the authors should be aware that the observation of strong dimerization may invalidate the use of FRET-based tension sensors in this system or at least necessitate intermolecular FRET control experiments.

We thank the reviewer for raising this important point. We agree that we lack direct evidence for the dimerization of vinculin in cells. Therefore, we have replaced “dimerization” with “the ability to dimerize” wherever it is relevant in the revised version of our manuscript, to emphasize that the ability to dimerize does not imply dimerization. The effects of the YE mutant may then be attributed to a lack of proper dimerization, or to any other, yet to be discovered defect dependent on the mutation but independent of the loss of the ability to dimerize. We have added a sentence in the discussion to account for this possibility:

"Whether vinculin dimerization, or another unknown independent function disabled by the YE mutation or phosphorylation of Y1065, is specifically involved in the adhesion and migration phenotypes described above may be addressed in future studies."

We thank the reviewer for suggesting experimental strategies to assess vinculin dimerization in cells. In another work, we have evidenced proximity by intermolecular FRET in FAs between proteins with no known interacting domains (doi: 10.64898/2026.04.22.720102). This raises the possibility that FRET, as well as split-GFP and PLA, the detection ranges of which are equal or larger than FRET, will not be able to discriminate between bona-fide direct interactions and very close proximity in environments such as adhesion complexes where protein densities are very high. As pointed out by the reviewer, this is the major reason why we preferred not to carry the experiments in the present paper in a null background, such that the endogenous vinculin can prevent intermolecular FRET between neighboring sensors, as we explain in the Materials and Methods.

Despite this methodological challenge, indirect evidence is largely in favor of dimerization in cells rather than against it, as explained below.

- While there are indeed many actin binding proteins in cells, the proposed scenario by which they would prevent vinculin dimerization by competing with vinculin for actin binding seems very unlikely to us. Indeed, according to this scenario, vinculin would also fail to be under tension, since it needs to bind to actin for that. We show here, as many others did before, that vinculin is under tension, implying that it is able to bind to actin. Therefore, vinculin-bound actin may subsequently facilitate vinculin dimerization.

- Additionally, vinculin also dimerizes in the absence of actin in solution, albeit at higher concentrations than in the presence of actin, equivalent to at least 0.1 molecule per 100nm² in any 2D section of the volume (doi: 10.1074/jbc.M111.244293, 10.1021/bi801764a). The density of vinculin within adhesions is promoted by the multiple neighboring vinculin-binding sites on its partners (such as talin, in which the neighboring binding sites are occupied nearly all at once upon talin stretch, doi:10.1021/acs.nanolett.6b00650, 10.1039/c5ib00307e), and is likely to reach a molecule per 100nm² in order to accommodate the traction forces that cells exert on their substrates (doi: 10.1021/acs.nanolett.6b04364). This exceeds the threshold concentration for vinculin dimerization in the absence of actin by at least an order of magnitude, and is therefore likely to offer another route for vinculin dimerization in addition to actin binding.

- Furthermore, Huang et al have shown that Y1065 phosphorylation is required for the activation of vinculin, and the YE mutant mimics this behavior, but they have also shown that the activation level is quite similar to that of WT vinculin (compared to the loss of activation of the YA mutant). Additionally, phosphorylation or the YE mutation does not abolish the head-tail interaction of vinculin, as shown by Küpper et al. (doi: 10.1016/j.bbrc.2010.07.110), who also show that YE is less stable in FAs, in agreement with our results. Altogether, these results support a model by which pY1065 is required for vinculin activation but facilitates its inactivation and release from FAs, which is easily explained if dimerization, which antagonizes head-tail interaction, is impaired.

In conclusion, in the absence of identified mechanisms to oppose vinculin dimerization in cells, and to better explain the observed phenotypes at the cellular level, vinculin dimerization in cells remains the most parsimonious scenario. We have added the following sentence to account for this:

"Nevertheless, vinculin dimerization, with its ability to antagonize its head-tail interaction and to promote actin bundling, remains the most parsimonious mechanism that can explain the stabilization of vinculin in FAs and the stiffening of cells described here and elsewhere (Tolbert et al. 2014, Küpper et al. 2010)."

(2) The authors have seemed to assume that FRAP and adhesion stability are interchangeable. To this reviewer’s knowledge, this is not the standard in the field. FRAP informs about molecular dynamics. Stability assays, which probe the spatial position of an entire focal adhesion over time (Zaidel-Bar, JCS, 2007, although other approaches are equally suitable), are typically used for assessing adhesion stability. If the authors wish to make strong claims about the stability of the adhesions, non-FRAP-based assays should be employed. Alternatively, the authors could interpret the FRAP data simply in terms of vinculin dynamics.

We agree with the reviewer. We did not wish to make claims about the positional stability of adhesions as a whole, therefore, we now specify “molecular stability” wherever needed in the revised version of the manuscript, to reflect that we refer to the stability of the molecular components of adhesions. We use the immobile fraction of vinculin and its mutants as a measure of vinculin stability and, by extension of the molecular stability of adhesions, because the stability of other adhesion proteins is dependent on the stability of vinculin, as supported by the various references we cite in the text (Carisey et al. 2013, Liu et al. 2016, Yonemura et al. 2010).

(3) A major conclusion in the manuscript is that in response to overexpression of a specific vinculin construct, focal adhesions behave the same in single cells, confluent cells, and collectively migrating cells for all the mutants but Y1065E. However, outside of the FRET measurements, there is not much evidence to support this claim. The authors should perform a greater comparison of the focal adhesions between the systems used in the manuscript (single cell, confluent cells, collectively migrating cells). Key measurements would include focal adhesion number per cell, focal adhesion size, focal adhesion orientation, vinculin dynamics (e.g., FRAP), focal adhesion stability, and some indicators of focal adhesion composition. For the last aspect, focusing on focal adhesion components that also have roles in adherens junctions, such as VASP, seems appropriate. Without such characterization, it is an overinterpretation to assume that focal adhesions are the same in each system and, therefore, effects are due to vinculin behavior in the adherens junctions.

We thank the reviewer for raising this point. We do not assume or need to assume that FAs are the same in single cells, at confluence or during directed migration. The simplest model that explains our results, however, does imply that the response of FAs to a given construct is the the same whether cells are single, at confluence or involved in directed migration. We explain below our approach:

- First, we show that the migration speeds of WT, FL, TL, T12 but not YE cells at confluence are predictable from their migration speed as single cells (Fig. S4C). Roughly, v_c ≈ v_s _−_10(_µ_m/h) for all but YE.

- From here, there are two possible scenarios:

(A) Each construct has the same effect on cell speed in single cells and at confluence through FAs, and AJs provide an additional downregulation of ≈ 10µm/h for all the constructs except YE. This implies that the mutants (except YE) have no effect on cell speed through AJs, since confluence induces the same decrease of ≈ 10µm/h in mutant cells as in FL or WT cells, in which vinculin is not mutated.

(B) One or several mutants have different effects through FAs on cell speed between single cells and at confluence, and there is an additional effect of AJs on migration that depends on the mutant and that compensates for the difference in the effect of the mutant through FAs between single and confluent cells, such as to preserve the observed v_c ≈ v_s −10(µm/h). For instance, compared to WT, T12 could increase the speed of 15µm/h in single cells and of 15−xµm/h at confluence through FAs, but decrease it of 10+xµm/h through AJs to compensate. It is already straightforward that this scenario, which adds one unknown parameter per mutant, is the least parsimonious. It would require as many additional pieces of evidence to be considered equally likely as the first scenario.

- If we review the effects of the mutants (except YE), there is no additional evidence in support of the second scenario: overall, mutants have similar effects on tension in FAs of single and confluent cells, as well as in AJs (Fig. 2D, 4D,E, S4G). They also have similar effects on stability in FAs and in AJs (Fig. 2E, 4F).

- As a matter of fact, we do not exclude the possibility that the mutants have different effects in single and confluent cells on other FA properties. In light of the above, however, the principle of parsimony requires that evidence for 1) such differences and 2) their impact on cell speed be brought first before we can consider the second scenario equally plausible.

In summary, there is no need nor other reason for x to be substantially different from 0 for any mutant, and YE is the only mutant for which there is a need for a specific contribution through AJs distinct from the other mutants to explain its difference in speed between single cells and confluent cells. We have now added a quantitative analysis of how this difference in speed changes across mutants (Fig. S4F and Materials and Methods). Results show that a power law provides an excellent description: the speed difference only depends on the molecular stability and not on the tension in AJs, and it is very weakly sensitive to the changes in stability between FL, TL and T12 while very sensitive to the low stability reached by YE. We detail this analysis below in response to Question 6.

(4) What is shown in Figure 3G is not clear. How are P/Po and alpha shown on different areas of the same plot?

We are sorry that our plot was not clear enough. For any given pair of simulation coordinates P₀/τ and n=πρd², the simulation yields either a persistent random walk or a super-diffusion behavior, based on the Akaike Information Criterion. Simulations show that the vast majority of the points that yield a persistent random walk (in blue) are grouped on the low density side of the plot, and the vast majority of the points that yield a super-diffusion behavior (in orange) are grouped on the high density side of the plot, typical of a system with two distinct phases within the space defined by the simulation parameters. Within each phase, each migration behavior changes as a function of the simulation parameters, these changes are quantified through either P/Po or alpha according to the most likely migration behavior of the phase. Of note, there are 3 regions of slight overlap: very low persistence (bottom line), very high persistence (top line) and the boundary between the two sides of the plot, because the finite number of simulation repeats (5) for each coordinate and their intrinsic stochasticity do not allow us to discriminate the two behaviors when their difference becomes smaller in these regions. Nevertheless, it is possible to determine the most probable behavior for each point and its close neighbors at the cost of some resolution, which results in a boundary that is slightly scaled rather than smooth if one looks closely. We consider that this is sufficient resolution for the purpose of this study. Our procedure is explained in detail in the Materials and Methods section. We have added a reference to this section in the figure legend for clarity.

(5) It seems that an insufficient statistical test was used in many experiments. There are comparisons being made between systems (cell migration speed, FRET index...) that are not directly compared in a statistical test. Statistical tests are limited to differences from control (over-expression of full-length vinculin), and consistent increases or decreases (not quantitative values) are taken as evidence of similarity across systems. It seems that a more rigorous and standard approach would be to use an ANOVA/MANOVA with a suitable post-hoc test to perform all of these.

We thank the reviewer for these suggestions.

- For comparisons within a system (between migration speeds only, or between FRET index only...), we selected a priori the most sensible comparisons for our analysis: between the control FL and mutants (Fig. 2B-E, 4B-F), or between front and back cells for each constructs (Fig. 6C,E). To account for multiple comparisons of FRET to FL, we have now re-analysed our data with non-parametric Kruskal-Wallis and unpaired, two-tailed Dunn’s tests, and applied corrections to the p-values with the Benjamini-Krieger-Yekutieli (BKY) two-stage step-up FDR procedure after a check for positive dependency between comparisons by bootstrapping. To account for multiple comparisons of immobile fractions in FRAP experiments, we applied the same BKY corrections to p-values obtained from fit comparisons. To account for multiple comparisons of FRET between front and back cells, we applied the same BKY corrections to p-values obtained from Mann-Whitney tests since none of the comparisons shared any condition. Overall, the corrections resulted in marginal changes in p-values that did not alter our conclusions.

- For comparisons of effects between systems (migration speed vs FRET index...), MANOVA and related approaches are not suited for comparisons between system-level means with different statistical units between systems. To account for effect sizes, we instead performed Pearson correlations or linear regressions, assuming a linear relationship between effect sizes from different systems (Fig. 6A, S2D-G, S4C,H). This allowed us to identify whether mutants have quantitatively similar effects in different systems and which of the mutants do not. Specifically, this is how we identified the YE mutant as different.

- Finally, to quantitatively support our Boolean models of speed dependence on tension, stability and tension gradients (Fig. 2F, 4G, 6F), which binarized the output of each system for the sake of simplicity (fast/slow, tensed/relaxed, stable/unstable, mechanosensitive/insensitive), we have now performed additional regression analyzes between re-scaled data (as detailed in the Materials and Methods). This allows us to quantify the contributions of changes in tension, stability, and the gradients of tension to changes in single cell migration speed, in the difference between single and collective cell migration speed, and in the ratio between collective cell migration speed and wound healing rate. As shown in the added Fig. S2I, the change in single cell speed is explained by a linear combination of changes in tension and stability with contributions of 2_/3 and 1/_3, respectively. In Fig. S4F, the difference between single and collective cell migration speed changes with the stability exclusively, and its increased sensitivity to low stability is well captured by a power law. In fig. S5C, the ratio between collective cell migration speed and wound healing rate is set by the difference in mechanosensitivity between FAs and AJs in which 1/3 of that of AJs counts. Overall, these results confirm our initial binary models.

(6) It is unclear how a lack of vinculin dimerization at adherences junctions perturbs epithelial migration, but the complete lack of vinculin tail, which can also not dimerize, does not. In other words, how can TL "have no other role in cell migration at confluence than those at FAs as in single cells." Notably, the authors do not include the tailless variation in the schematic model figures. These results should be included and explained.

We are sorry that we lacked clarity. Here was our reasoning:

Both the YE and TL mutants are indeed impaired for dimerization but they differ in two ways:

- YE binds actin and is under tension while TL does not.

- YE is not impaired for head-tail interaction and not stable while TL is.

To determine which of these properties affect cell migration, we first compared YE to the other constructs. Just like YE, FL and T12 also bind actin and are under tension, but the migration speeds of FL and T12 cells at confluence can be predicted from their migration speed as single cells, unlike YE. Therefore, tension is unlikely to explain why YE has an effect on migration speed at confluence not predictable from single cell speed. The irrelevance of tension for the scaling of single to collective cell migration speed is also consistent with the fact that TL lacks tension but still obeys the same relationship as FL and T12 between single and collective cell migration speed. Furthermore, FL and T12 also share with TL their stability in adhesions, unlike YE. The instability of YE is then likely to explain its peculiar effect on migration behavior, because this is the only feature that differentiates YE from all the other constructs, TL included. The Boolean models in Fig. 4G and elsewhere are meant to show within a Venn diagram the main molecular conformations and associated interactions of intact vinculin, and their individual and combined consequences at the adhesion and migration level. We have now specified this is the figure legends of the revised manuscript. There is no 1-to-1 mapping of each mutant to one particular conformation of the intact vinculin. Rather, the effects of the mutations on each conformation are specifically indicated in Fig. S2A.

In support of this model, we have added in the revised manuscript a corresponding quantitative analysis, as mentioned in response to Question 3 and 5. Briefly, we first looked for the optimal linear combination of change in tension and stability that could explain the change in the difference between single and confluent migration speed across vinculin constructs. This step excluded tension as a significant contributor to the speed difference. We then looked for a relationship that was an as simple as a weighted combination of two terms (i.e. with only 1 adjustable parameter) that related the changes in speed difference to those in stability only, and found the power law dependence on stability. These results, which confirm our initial analysis, are shown in Fig. S4F. Notably, they show that 1) none of the constructs have an effect on the speed difference between single and confluent cells through tension, and 2) the changes in stability across TL, FL and T12 have a minimal impact on this difference, only that between YE and the others has an impact, as highlighted by the small exponent of the power law. Overall, this is consistent with a model whereby the migration speed of cells at confluence is largely predictable from their migration speed as individuals for WT, FL, TL and T12 (Fig. S4C), with an effect of the mutants TL and T12 similar to that of the unmutated FL. The most parsimonious explanation is that the effects of those constructs on cell speed at confluence are explained by the same mechanisms as their effects on cell speed in single cells, that is, through their FAs, and that the effects of TL and T12 through AJs are not much different from that of FL, meaning that the mutations have no other role in cell migration speed at confluence than those at FAs as in single cells. We have slightly modified this sentence as above in the text to specify that the lack of effect of these mutations on migration is on migration speed specifically, not that they have no effect whatsoever.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

In general, I would suggest that you properly define all notions that you use. Notably, you should explicitly introduce basic concepts like the Furth model, Lévy flight, fractional Brownian motion, the shape index, and others. It gives you the possibility to introduce your notation. For the readers, it would make your manuscript more accessible as they would not need to look up these notions elsewhere. The following points and questions are not exhaustive, but might serve as a guide to improve your write-up.

We thank the reviewer for this suggestion, we have modified the text in the main manuscript to explain the notions in plain English and have added references to the Material and Methods for the more formal definitions, mathematical formulations and additional explanations whenever appropriate. All the modifications are highlighted in the revised manuscript. We hope this revised version will make our manuscript clearer.

You should give the parameter values for all fits that you provide. Table S1 should give them, if I understand correctly, but in the version I have, this table only provides p-values.

We have now added the fit parameters in Table S1 in the revised version. They are also displayed in Fig. S2D and discussed in the associated text.

Why is vinculin or FA stability related to the immobile fraction in FRAP experiments? I would suggest speaking about vinculin or FA lifetimes as measured by the characteristic recovery time obtained from FRAP. How do you interpret the immobile fraction? Do you think that there is an FA ’core’ that persists until the FA is dissolved? In that case, the immobile fraction would report on the relative core size of the FA.

We indeed consider that this is the amount of protein that remains the longer that is the most relevant to assess the molecular stability of adhesions and its impact on migration, because an adhesion must disassemble entirely to allow cell displacement away from that site.

In Figure 1B, the fits of the exponents are not very convincing, and they extend over as they cover hardly one order of magnitude.

We are sorry that figure was misleading. The extreme slopes of 2 and 1 were not meant to indicate the actual time windows where ballistic and pure diffusion would actually be observed but just the values toward which experimental data would tend at short and long lag times, respectively, for a persistent random walk. We hope the new version of the figure in the revised manuscript will clarify this. Additionally, while the range indeed appears short, it is largely sufficient to discriminate between persistent random walk and pure or anomalous diffusion based on the Akaike Information criterion, which is the quantitative and objective metric we exclusively use throughout this work to discriminate between migration behaviors. The scores range from 0 (pure or anomalous diffusion) to 1 (persistent random walk) and table S1 shows that Fig. 1B (among others) is unambiguously a persistent random walk, even within this limited fitting range.

Figure 2B, D, what do the stars indicate?

Stars indicate p-values. We now explain this in the figure legends in the revised version of the manuscript.

Please explain how the FRET index is related to stress?

We are sorry that we had overlooked this important explanation. We have now added explanations in the main text and in the Material and Methods. Figures now also include the direction along which the tension increases when FRET changes.

"This shows that impaired head-tail interaction, regardless of tension, is sufficient for vinculin stability." Sorry, but I do not understand what you mean.

We are sorry that we lacked clarity. We have modified this sentence as follows in the revised manuscript: “This shows that impaired head-tail interaction, whether associated with impaired actin-binding (TL) or increased tension (T12), is sufficient for vinculin stability with FAs.”

I would avoid the term angular memory. You might use a correlation time, that is, fit the curve to an exponential and take the corresponding characteristic time as a measure for persistence.

We thank the reviewer for this suggestion. The reason why we introduced this metric was not to extract a persistence time, which we already obtained from the MSD, but to provide compelling evidence that the super-diffusive behavior at confluence arises from a fractional Brownian motion, rather than from another type of super-diffusive walk. We now provide in the revised manuscript a more detailed explanation of this metric, why we prefer it to the more conventional velocity auto-correlation function for our purpose, along with its formal mathematical definition, as explained below. The angular memory is a modified angular correlation in which we consider the angular deviation θ of each elementary step of duration 10min from its immediate previous step of duration τ equal to the lag time ∆t. Specifically, the angular memory M_i,t(∆t) of a cell i at time t is the cosine of the angle θ_i,t between consecutive step vectors between times t−∆t and t and between times t and t+10min, such that the step duration τ of the first vector and lag time ∆t before the next are equal. M_i,t(∆t) = cosθ_i,t(∆t) = cos. This metric measures the duration of the past that the cell considers when deciding on its direction. It decays to 0 when ∆t → ∞ for persistent random walkers and remains constant for fractional Brownian motion, similarly to the auto-covariance function of fractional Brownian motion C(∆t/τ) = ((∆t/τ +1)^𝛼 +|∆t/τ −1|^𝛼 −2(∆t/τ)^𝛼)/2, which is a constant C \= 2^𝛼-1−1 for all ∆t \= τ, as in our definition of angular memory (while also decaying to 0 when ∆t/τ → ∞) (Metzler et al. 2025). Ballistic motion yields 1 whatever ∆t and uncorrelated random walks, whether anomalous or not, yield 0. For this reason, and because M_i,t(∆t) was found more robust to noise than C(∆t/τ), we considered this metric a more compelling discriminant between fractional Brownian motion and other uncorrelated super-diffusive walks. Consistently, we found that the angular memory of single cells decayed to 0 while that of confluent cells did not and remained nearly constant within our experimental time frame.

(Of Note, we have increased the analysed data set in the revised Fig. 1D, 3D,F for the sake of representativeness. The conclusions are unchanged).

"While cells adopt a superdiffusive behavior at confluence, they do so in any possible direction." Sorry, but I do not understand what you mean.

We are sorry we were not clear. We changed the sentence as follows : “While cells adopt a super-diffusive behavior at confluence, they do so in the absence of any external guidance cue, and as a consequence without any preferred direction.”

Reviewer #3 (Recommendations for the authors):

(1) The authors have chosen to use an overexpression system. That means that wild-type vinculin is competing with the mutant vinculin in many cases. Also, the authors have chosen not to study a phospho-deficient form of vinculin or manipulate vinculin dimerization in any other way. Given that these are not the most rigorous experiment set-ups and designs possible, the authors may wish to lessen the strength of some of their conclusions.

This is correct. We have added in the discussion the following sentence to account for the possible contribution of consequences of the YE mutation other than dimerization impairment, and for the presence of the endogenous vinculin:

“Whether vinculin dimerization, or another unknown independent function disabled by the YE mutation or phosphorylation of Y1065, is specifically involved in the adhesion and migration phenotypes described above may be addressed in future studies. Likewise, whether the effects are stronger in the absence of endogenous vinculin may be addressed in a null background.” Additionally, we have modified the text throughout to change "dimerization" into "the ability to dimerize".

(2) Dominant effects have been shown for T12 and VinTL; however, to this reviewer’s knowledge, dominant effects have not been shown for vinculin Y1065E.

This is correct, we now specify it in the revised version.

(3) This statement: "Overall, this is consistent with the idea that vinculin acts primarily as a migration moderator, and this supports that insertion of the sensor module weakens to some extent the auto-inhibition of vinculin, thereby contributing to the dominance of all exogenous constructs over endogenous vinculin, in addition to the effects of their mutations" lacks experimental support. Multiple studies have shown that the effects of the insertion of the tension-sensitive module are small on vinculin, including demonstrations that FRAP recovery is unaltered. To make this statement, the authors should perform comparisons of vinculin and vinculin mutants with and without a tension sensor. If differences are observed, it seems that experiments in the manuscript should be repeated with vinculin mutants not harboring a tension sensor. If the presence of the sensor affects mutant behavior, then it seems unlikely that the claims of the paper are correct. For instance, it would suggest that vinculin dimerization is not the sole driver of the velocity coupling, instead it could be a combination of partial activation and lack of dimerization. Alternatively, the authors could remove or edit this sentence.

We agree that the second part of our statement was incorrect and have removed it. We cannot say that the insertion of the sensor module weakens the auto-inhibition and we agree that there is no difference in turnover compared to a vinculin construct without the sensor.

(4) Vinculin dimerization is drawn incorrectly in many of the schematic figures summarizing results. Vinculin dimerization is dependent on F-actin binding (see work of Sharon Campbell and others). Vinculin is unlikely to form a "dimer" in solution, as shown in these schematics. Also, vinculin dimers are thought to form along the length of two bundled actin filaments, not at the end, as drawn in the schematics.

We thank the reviewer for these suggestions. Sharon Campbell and others have indeed shown that actin binding promotes the dimerization of vinculin tails in solution. They and others have shown, however, that vinculin tails also form dimers in the absence of actin, albeit at higher concentrations, which are equivalent to at least 0.1 molecule per 100nm² in any 2D section of the volume (DOI: 10.1074/jbc.M111.244293, 10.1021/bi801764a). The density of vinculin within adhesions is promoted by the multiple neighboring vinculin-binding sites on its partners (such as talin, in which the neighboring binding sites are occupied nearly all at once upon talin stretch, doi:10.1021/acs.nanolett.6b00650, 10.1039/c5ib00307e), and is likely to reach a molecule per 100nm² in order to accommodate the traction forces that cells exert on their substrates (doi: 10.1021/acs.nanolett.6b04364). This exceeds the threshold concentration for vinculin dimerization in the absence of actin by at least an order of magnitude, and is therefore likely to offer another route for vinculin dimerization in addition to actin binding. We conclude that vinculin density in adhesions is very likely to allow dimerization in the absence of actin, and the binding to actin additionally promotes dimerization. Due to the omnipresence of actin in adhesions, the dimer unbound to actin certainly accounts for a small fraction of possible vinculin conformations, but this is likely to be very context-dependent and current knowledge is too limited to be more quantitative. We have therefore decided to keep our model simple with all these possible conformations, without indications of their possible proportions.

We agree that the drawing of the interaction with actin does not properly depict the side-binding of actin and we have modified it in the revised version. Nevertheless, vinculin and actin are known to bind by both their sides and ends (DOI: 10.1074/jbc.M110.102830).

(5) Technically, the authors have not shown that conservation of angular momentum is "infinite". It just appears longer than the experimentally accessible terms. The use of term short-lived and long-lived, instead of finite and infinite, might be more appropriate.

We agree, we have changed “virtually infinite” to “long-term” everywhere in the text to avoid confusion.

(6) The conclusions of the manuscript seem to treat vinculin loading and vinculin stability as independently regulated. However, vinculin has been shown to act as a catch, both in vitro (see work of Alex Dunn) and in living cells (see work of Sharon Campbell), suggesting strong coupling of these quantities. A discussion of the points would benefit the manuscript.

We agree that vinculin loading and stability in adhesions depend on each other and thank the reviewer for suggesting these additional references. We formulate our model as follows: “Mechanistically, our results support that the head-tail interaction of vinculin challenges both force transmission and stability of vinculin in FAs, as has been observed in other cell types (Carisey et al. 2013, Humphries et al. 2007, Cohen et al. 2006, Dumbauld et al. 2013, Liu et al. 2016, Omachi et al. 2017)...” This shared dependence and factors that independently affect force transmission or stability, but indirectly feed back to each other, are not mutually exclusive, as we state next: “... and is countered by the actin-vinculin tail interaction, which provides force transmission but is unnecessary for stability, and the ability of the tail to dimerize, which associates with higher stability and is dispensable for force transmission (Fig. 2D,E).”

Such feedback implies that the interaction between actin and the tail of vinculin can promote stability, even though it is not necessary for this (as shown with TL), and that the ability of the tail of vinculin to dimerize can promote force transmission, even though it is not necessary for this (as shown with YE). We have added the following sentence in the revised version to clarify this point:

“As a result of this feedback, stability and force transmission can be further promoted by the interaction of the vinculin tail with actin and its ability to dimerize, respectively, indirectly through their antagonism with the head-tail interaction of vinculin.” Consequently, this opens the possibility that a catch-bond between vinculin and actin also promotes vinculin stability in adhesions, which is indeed shown by the Campbell lab (doi:10.1038/s41467-023-43779-x), thanks to a prolonged antagonism with the head-tail interaction. Interestingly, their results show that the ability to form a catch bond does not appear to oppose the head-tail interaction more than actin binding does (their Fig. S10). This suggests that the actin-vinculin catch bond stabilizes vinculin in adhesions through a mechanism that has yet to be identified. In conclusion, vinculin loading and stability in adhesions are interdependent through the head-tail interaction and through another unknown mechanism that involves the catch bond between vinculin tail and actin. We now include a sentence that refers to this catch bond in the revised manuscript.

(7) Recently, two papers have come out assessing the role of AJs and mechanical coupling during epithelial migration: Noordstra, Dev Cell, 2023, and Shoyer, PNAS, 2023. Comparing the results of this manuscript to those of these publications would strengthen the discussion.

We thank the reviewer for suggesting these references.

Noordstra et al provides a very interesting investigation of the mechanisms whereby the mechanosensitive alpha-catenin down-regulates lamellipodial activity in epithelial sheets that form intercellular contacts during wound closure. This could offer a potential mechanism that would explain why we observe that cells at confluence migrate at a lower speed than single cells. While a minimal lamellipodial activity is indeed required for cell migration, we have previously shown, however, that the down-regulation of lamellipodial activity by the formation of AJs does not decrease cell migration speed (doi:10.1073/pnas.1002662107), but the formation of desmosomes does (doi:10.1242/jcs.146316). We have included these considerations in the discussion of the revised manuscript.

The main finding Shoyer et al is that the phosphomimetic mutant S1033D of vinculin relaxes vinculin tension and reverts it to a close conformation in both AJs and FAs. The mutant affects directed collective cell migration in a manner that preserves the relationship between lateral velocity deviation amplitude and coordination length but consequences on vinculin stability in adhesions, or on single and undirected collective migration are unknown. Thus, it would be worth assessing them to determine whether this mutant affects cell migration through FAs, AJs or both, and how it fits in our model. We have now included this reference in the discussion of our revised manuscript.

[Editors' note: The authors included an author response to reviews from another journal]

Reviewer #1 (Comments to the Authors):

In this manuscript the authors describe that cells in collective movements adopt a superdiffusive behavior to out pace individual cells. This behavior is regulated by cell-cell junctional stability and force transmission. The authors state that speed is regulated by vinculin through mechanosensitivity.

While is makes intuitive sense that cells may move more efficiently collectively as it reduces their exploratory space and therefore increases their efficiency of movement,

We agree that this is an intuitive explanation. However, previous literature had shown that confluent cells may or may not migrate depending on conditions that do not solely depend on the space available per cell, but also involve the intrinsic activity of the cell, its cortical tension, and its adhesion with its neighbors, with sometimes counterintuitive effects (doi: 10.1016/J.CEB.2021.07.011). This was the reason that motivated us to investigate how these various ingredients affected space exploration efficiency on different time scales.

Our results indeed refute the intuition that cells move more efficiently when their exploratory space is reduced by showing that the outcome depends on the time scale considered (Fig. S3B). Specifically, on short time scales (less than 3 hours), the area explored by individual MDCK cells is larger than that explored by MDCK cells at confluence. On a longer time scale (greater than 3 hours), however, the area explored by confluent MDCK cells is larger. This switch is a direct consequence of the change in migratory behavior from persistent random walk to superdiffusion, Moreover, its position in time depends on the cell line: extrapolation of our results on RPE-1 cells suggests that it should theoretically occur after approximately 300hrs, if this time scale was experimentally accessible (Fig. S3F).

…the role of junctions specifically is less clear.

We are sorry that we were not able to clearly convey the roles of junctions. We have substantially rewritten our text to address this and all the changes are highlighted in orange. As summarized in Fig. 6F, junctions have three roles. The first role is on persistence, through velocity coordination between neighbors, the second is on speed, through the stability of junctions, and the third role is on directionality, through the sensitivity of the monolayer to the wound edge.

The first role is evidenced thanks to the comparison of the MSD between single cell and confluent migration assays and the use of the alpha-catenin KD cell line. Alpha-catenin depletion is known to be the most potent disruptor of adherens junctions (DOI:10.1091/mbc.e06-05-0471, , DOI:10.1126/science.aaf7119, (DOI:10.1073/pnas.1002662107, DOI:10.1073/pnas.1119313109), and we show that it significantly alters the superdiffusive behavior that emerges in the confluent migration assay (Fig. 3E,F, 5C). Therefore, junction integrity is critical for the control of cell persistence.

Moreover, alpha-catenin depletion induces a loss of velocity coordination between neighbors (Fig. S3E), which we show through numerical simulations to induce superdiffusion (Fig. 3G). By contrast, E-cadherin KO and vinculin mutants have no effect on the superdiffusion of confluent cells (Fig. 3E, 4A). Therefore, the critical molecular ingredient is the link provided by alpha-catenin to the cytoskeleton that provides junction integrity.

The second role of junctions is evidenced thanks to the comparison of cell speeds between single and confluent migration assays with the vinculin mutants (Fig. S4A). Results show that cell speed is reduced of about 10µm/h by confluence, regardless of the mutant except for YE, whose only difference with other mutants is its lower stability (Fig. 4F). This supports that junction stability, and not the other effects of mutants, controls cell speed (we provide a detailed demonstration in the response to the following question). As expected, junction integrity is required as well, as seen from the higher cell speed of the alpha-catenin KD cell line compared to WT (first MSD point in Fig. 3B, E).

The third role of junctions is evidenced thanks to the comparison between confluent and directed migration assays (Fig. 6A). Results show that the wound healing rate is proportional to cell speed at confluence, regardless of the mutant except for YE, which displays no tension gradient in junctions from front to back cells (Fig. 6C). This supports that such gradient is required for cells to identify on which side is the wound edge. As expected, junction integrity is required as well, as seen from the loss of directional bias of the alpha-catenin KD cell line (Fig. 5F).

The authors chose vinculin as the basis by which to manipulate tensions at cell-cell junctions, but this comes with considerable drawbacks. Namely, since vinculin appears at both cell-cell and cell-matrix junctions, its role and the role of its mutations is not clear here. The authors state that the collective migration speed is related to junctional stability, but because vinculin is also at FA, how can this be concluded?

We apologize for the lack of clarity. We hope that the highlighted changes in the revised manuscript will improve this point. As exemplified above, comparing cell migration between isolated cells and confluent cells is essential to enable us to distinguish between the contributions of AJs and FAs. Indeed, since isolated cells lack AJs, the impact of vinculin mutants on single cell migration can only be explained by their effects on FAs. This is how we first determine the effects of vinculin mutants on migration that depend on FAs. Because confluent cells also have FAs, we expect that the effects of vinculin mutants on the migration of isolated cells will still be present in confluent cells, to which will be added the effects of these mutants on AJs and their consequences on migration, if any.

Therefore, when compared to WT cells, if a given mutant decreases or increases migration speed in individual cells, and does so in confluent cells in the same proportion, then its effects at confluence can be entirely explained by its effects in individual cells, and there are no additional effects of that mutant from AJs. This is indeed what we observe for all mutants except the YE mutant (Fig. S4C), leading us to conclude that none of the vinculin mutants, except the YE mutant, have an effect on migration at confluence that results from AJs. In contrast, the YE mutant has effects on migration at confluence that cannot be explained by its effect on individual cell migration. Therefore, the effects of YE at confluence depend on AJs, whether they result from alterations in AJs, FAs, or both. To distinguish between these scenarios, we proceed by elimination, comparing the effects of YE to those of other mutants on force transmission and adhesion stability, and how these two factors associate with migration speed, as explained below. In FAs, YE alters force transmission differently in individual cells and at confluence, but we already know from Fig. 2 that force transmission in FAs cannot alone explain the speed of migration. This result rules out an indirect effect of AJs on cell migration at confluence through FAs. Furthermore, in AJs, YE affects stability and force transmission, but TL has the same effect on force transmission as YE and we already know that none of the effects of TL on migration depend on AJs (Fig. 3, S4C). This result rules out an effect of force transmission in AJs on migration speed at confluence. We conclude that stability at the AJ level, which is the remaining property specifically impaired by YE, is what regulates migration speed at confluence.

The manuscript's logic and flow are not clear in some places, making the story hard to follow. As one example, the FRAP data, which the authors suggest is used to investigate vinculin's combined role does not help in this capacity as the interpretation and its connection to the bigger story are not clear.

We are sorry again for the lack of clarity. We used FRAP data to evaluate the effects of vinculin mutants on adhesion stability. Indeed, mutants have different effects on adhesion stability (Fig. 2E, 4F). In addition, they also have different effects on force transmission (Fig. 2D, 4D,E). The partial overlap in functional alterations caused by the mutants allows us to test the involvement of the overlapping function (here stability) in the overall migration outcome. For example, if two mutants have a similar effect on adhesion stability but different effects on migration speed (such as TL and T12), we can then rule out that speed results from adhesion stability. Similarly, if two mutants have different effects on stability but a similar effect on speed (such as TL and YE), we can also rule out that speed results from stability. We applied the same reasoning to force transmission to conclude that neither adhesion stability nor force transmission alone is sufficient for cells to migrate rapidly. However, the combination of the two enables rapid migration.

As another example, the information derived from the use of the mutants is not clear in the context of the message in the manuscript since they affect cell-cell and cell-matrix junctions and in some places show results that are counter intuitive and not well-explained, to which the authors admit they are surprising but then do not explain their meaning.

As such, it is very hard to follow the logic with regard to the information resulting from the mutant experiments.

We provide above a detailed break-down of our strategy to analyze the results. We regret that our manuscript did not adequately convey our conclusions and we hope that the new version of the manuscript improves this point.

Proliferation has been shown to play a role in wound healing. Does proliferation change in the various conditions?

This is an important point. The average speed of cells at confluence is approximately 20 µm/h (Fig. 4B), which means that each cell moves approximately its own size in one hour. During this time, assuming a 16-hour cell cycle, 6% of the cells would have divided, each of them likely pushing one of its neighbors a distance equivalent to the size of a cell. Therefore, cell proliferation accounts for at most a few percent of the total cell movement. For this reason, we can assume that growth does not account for a large part of the movement we observe. This is consistent with previous work showing that proliferation does not contribute significantly to wound healing (DOI: 10.1073/pnas.0705062104, DOI: 10.1083/jcb.201207148).

Minor comments:

The authors should provide a better description of the mutants: what does a tailless mutant not bind, or bind differently? More context is needed to help interpret the results. While the mutants have all been published on before, it would be helpful to have more information here so that the manuscript is easier to follow.

We are sorry that the information we provided was insufficient. We have now detailed the mutations to help the reader understand how interactions are altered.

Figure 1A is not necessary. Figure 1 overall is fairly predictable as there have been many papers using the persistent random walk as the best model to single cell migration (dating back to the early 1990's). The authors define a new term, angular memory, which they show decreases with increasing delta t as one would predict.

We acknowledge that persistent random walks have already been observed for individual cells, as in references 3-4 cited in the introduction. Nevertheless, we believe that Figure 1 is important because not all cells migrate as persistent random walkers when isolated. Some migrate in a more exotic manner, resulting in superdiffusive behavior, as in references 5-8 cited in the introduction. Since we observe superdiffusive behavior at confluence (Figure 2), it was therefore necessary to show whether or not single cells were superdiffusive too. We also use this figure to introduce angular memory, a measure that, to our knowledge, has never been used before. According to intuition, it decreases to 0 for persistent random walkers, just as another resembling measure, velocity autocorrelation, would do. However, the angular memory of fractional Brownian walkers does not vanish with increasing delta t (Fig. 3D), while velocity correlation would, just as that of persistent random walkers. This difference makes angular memory much more appropriate for distinguishing between the two migration behaviors, and prompted us to introduce it in the first figure as a reference.

In the wound healing assay, which cells were measured? Leading edge or interior, and does it matter?

Figure 5A shows that cells behave differently depending on their distance from the wound. This is because the traces shown correspond to the first few hours of the movie, during which the cells at the front begin to move first. Figure S5A shows the speed of the cells over time after the wound and indicates that the cells reach a stable speed after approximately 3 to 4 hours. Figure S5B shows the speed of the cells as a function of distance from the wound at steady state. These results show that the speed of the cells no longer depends on the distance from the wound at this stage. As indicated in the “Materials and Methods” section, we only considered time points beyond this stage for subsequent analyses of population-averaged MSD and velocity presented in Figure 5, so the location of cells at the front or rear was irrelevant.

Reviewer #2 (Comments to the Authors):

To migrate cells must spatially explore their environments, a process that is guided by intrinsic signals (adhesive and mechanical properties, etc) and extrinsic (gradient cues) signals. This exploration can occur on the single or multicellular level. In this study, the authors examine the effect of cell-cell interactions, guidance cues, and cell mechanics in the exploratory capacity of MDCK cells. The authors show that cell-cell adhesion provides a "infinite directional memory for migration" and cell speed is dependent upon the focal adhesion stability, cell mechanics, and the mobility of adherens junctions-these processes are modulated by vinculin.

My three major concerns with the manuscript are as follows:

(1) While there is potential new information about the role cell-cell junctions and guidance cues play in cell migration, there is not enough NEW insight presented. Rather the role of vinculin in these processes is expected given what is already known about its ability to control focal adhesion stability, mechanics, and adherens junctions.

We agree that our cell migration results make sense based on the effects of vinculin mutants on the stability and force transmission of adhesions. Nevertheless, we argue that this was not the only possible scenario. Indeed, we find that none of the effects of vinculin mutants on AJs (except YE) have an impact on cell migration (Fig. S4C). One might have expected that the increased stability provided by the TL and T12 mutants would reduce the speed of collective cell migration, just as the YE mutant increased cell speed due to its altered stability. This is not what we found, and this reveals a nonlinear relationship between AJ stability and migration speed that could be investigated more thoroughly in future studies. Another example is that the effects of the mutants on force transmission in AJs do not impact migration speed at confluence but do impact directed collective migration (Fig. 6). One might have expected that vinculin-mediated force transmission in AJs would impact collective migration, whether directed or not.

More importantly, we show that the role of intercellular adhesion in cell migration is more complex than expected. Indeed, it depends on the timescale considered: intercellular adhesion is detrimental to short-term spatial exploration and beneficial in the long term (Fig. S3B). Such a timescale-dependent behavior is impossible to predict from previously known effects of the mutants or other molecular considerations. Furthermore, we show that this behavior can be fully explained by the coordination of velocities between neighbors, which depends on intact connections between AJs and the cytoskeleton via alpha-catenin, but is independent of vinculin mutants that connect AJs to the cytoskeleton in parallel with alpha-catenin. One might have expected these connections to also have an impact on velocity coordination, and thus on spatial exploration, but we show that this is not the case (Fig. 3). Finally, we show that directed collective migration has a negligible impact on cell exploration at our experimental timescale (Fig. 5), whereas we initially expected the wound to make migration more ballistic. This reveals that such a directional signal affects spatial exploration at much longer timescales than expected.

Overall, our results quantify the outcome of competing effects and provide timescales at which one effect outweighs the other in influencing cell migration. We believe this is an original approach that provides substantial new insights into collective cell migration.

(2) The phenotypes of the cells expressing the mutant vinculins varying greatly. These phenotypes are not addressed despite the fact that they could potentially complicate the analyses. For example, there are dramatic differences between focal adhesion numbers and sizes in the cells expressing the different vinculin mutants; cell spreading is also dramatically altered. Likewise, the T12 mutant vinculin has previously been reported to have increased adhesive strength, increased traction forces, and cell spreading. How does this knowledge change the interpretation?

We agree that vinculin mutants may have effects on the size and number of FAs, cell spreading, and traction forces that we do not examine here. These consequences can be explained by the effects of these mutants on force transmission in FAs and on their stability, which we report in our work. They do not affect our interpretations. Here, we provide a predictive model of migration speed based on the combination of two consequences of vinculin function, namely stability and force transmission. An interesting avenue for future research would be to assess whether these combinations can be reduced to a single higherlevel effect of vinculin on the cellular phenotype that would be sufficient to predict migration speed. This work remains to be done, as neither FA size and number, cell spreading, adhesion force, nor traction forces alone are sufficient to predict migration speed.

Along the same lines, it has previously been established that tagged version of vinculin do not efficiently integrate into adherens junctions. Published work from the Nelson laboratory suggests that GFP-vinculins do not localize to cell-cell junctions and work from other laboratories suggests localization occurs only when the endogenous vinculin is silenced.

We are aware that some GFP-vinculin constructs may not localize as well as the endogenous protein at AJs. This is due to the localization of the GFP tag on the head of vinculin and depends on the length of the linker between GFP and the head of vinculin. The longer the linker, the easier the interaction with AJ partners. Unlike these constructs, the vinculinTSMod sensors we use in our work do not carry a GFP on the head and do not suffer from the same limitations.

Furthermore, vinculin recruitment to AJs depends on force, with little or no recruitment when tension on the AJs is relaxed (DOI: 10.1038/ncb2055). Vinculin recruitment has in fact already been used as an indicator of AJ tension in Drosophila (DOI: 10.1038/s41467-01807448-8). Consequently, the amount of vinculin visible at the AJs varies depending on the tension exerted on the AJs, which our results confirm: vinculin is more difficult to detect at the AJs in cells located at the front of a wound than in those located at the back (Fig. 6B), which is consistent with the difference in vinculin tension between front and back cells (Fig. 6C) and to the E-cadherin tension gradient between front and back cells (DOI: 10.1083/jcb.201706013). Overall, these results show that vinculin is not always easy to detect at AJs, but this is due to the properties of vinculin, which the constructs we use reproduce better than previous constructs (see also below).

The images in figure S2 and the prebleach images in figure S4 do not show convincing localization of the mutant vinculins to cell-cell adhesions. This is of special concern given that YE mutant protein hardly has any discernable localization to cell-cell junctions; additionally, none of the mutant proteins were tested for their ability to co-localize with adherens junction components. This raises the question if the parameters being examined and the conclusions drawn from them are affected by a difference in localization.

We agree that the recruitment of vinculin at intercellular contacts may be difficult to see.

Besides force-dependent effects mentioned above, other factors are involved. The images shown in Figures S2 and S4 are from live cells in which cytoplasmic vinculin is still present, and its level proportional to the mobility of vinculin. Indeed, the TL and T12 mutants show a more marked contrast between intercellular contacts and the cytoplasm, which is consistent with their greater stability at AJs (Fig. 4F). Conversely, YE shows lower contrast, which is consistent with the lower stability of this construct at AJs (Fig. 4F). The FL construct lies between the two. As a result, the cytoplasmic content can variably mask vinculin recruitment at the AJs depending on the mutant.

We have now performed additional quantifications of mutant recruitment at intercellular contacts as a function of distance from the basal surface of the cells and relative to their recruitment in FAs, in live cells. Results are shown in the new Fig. S4F. We find that all the constructs are recruited to intercellular contacts with a density that is at most half of that in FAs and that varies along the height. FL shows the highest density, localized more apically, consistent with the localization of an AJ-bound actin belt. The mutants appear to be more homogenously distributed along the height of the lateral surface, which may be explained by their impaired autoinhibition (TL, T12), or mechanosensitivity (YE). This variability also contributes to the difficulty in seeing vinculin recruitment in all cells in a single z-slice.

To confirm the proper recruitment of vinculin constructs to AJs we have performed immunofluorescence against alpha-catenin and phalloidin on each of the stable cell lines. Results are shown in the new Fig. S4D and E. In these experiments, cell permeabilization allows for the release of some of the cytoplasmic pool of vinculin, which highlights the recruitment of all vinculin constructs to intercellular contacts. There, all vinculin constructs colocalize with alpha-catenin and F-actin, as expected. Additionally, images displayed are maximum intensity projections to mitigate recruitment variability along the height.

Overall, our results clearly support the localization of vinculin at intercellular contacts, and the differences between the constructs are consistent with the effects of their mutations.

(3) There is a lack of new mechanistic insight. Conclusions are made about a role of vinculin dimerization. This conclusion appears to be based upon the usage of the mutant version of vinculin Y1065. Did the authors directly measure the ability of this mutant protein to dimerize? Is actin binding also affected.

The binding properties of the Y1065E mutant, including its dimerization and binding to actin, have already been characterized by other researchers (ref. 40 in our manuscript, as well as DOI:10.1111/j.1432-1033. 1997.01136.x or DOI: 10.1016/j.febslet.2013.02.042). We assumed that these properties are now well established and can be used to explain higher-level phenotypes that we show for the first time, to our knowledge.

Reviewer #3 (Comments to the Authors (Required)):

Canever et al. tracked two epithelial cell lines on collagen coated glass and showed that isolated cells (non confluent) move as persistent random walkers, whereas confluent monolayers migrate super diffusive, with long range directional memory. By systematically perturbing adhesion machinery they found that focal adhesion mutations mainly tune the speed of single cell tracks, but cannot create long range memory, while force bearing adherens junctions are essential for the super diffusive regime-genetically perturbing them collapses collective memory. These interesting results identify junctional tension as important to switch epithelial cells/sheets between individual and collective search modes - an important quantitative insight that is of clear relevance to cell biologists.

- The presented data is nicely quantitative and convincing, but I have subtle concerns about the generality of the findings. While the authors show that the differential behavior, they describe is not cell-line specific (MDCK, RPE), there are no experiments evaluating the generality of their conclusions across different matrix conditions. How are the measured migration parameters affected by matrix stiffness? Cell migration on collagen coated glass coverslips is a relatively narrow and artificial condition. How is the collective directional memory expected to behave on softer substrates? The generality of the conclusions could be strengthened by repeating measurements using hydrogels of varying stiff-ness. Further, it should be discussed to which tissues in the body the selected matrix conditions and migration modes plausibly apply.

We agree that the generality of our results and the relevance of glass-rigid substrates is an important point. In vivo, epithelial cells rest on a basement membrane with a typical stiffness of approximately 10 MPa, as demonstrated by experimental evaluations on various tissue explants, including renal glomeruli and Bruch's membrane, which are relevant to MDCK and RPE-1 cells (DOI: 10.1111/j.1742-4658.2007.05823.x, DOI: 10.1172/JCI106898, DOI:10.1038/eye.1987.35), we have added these references in the manuscript to support our experimental strategy. In vitro, the most significant effects of substrate stiffness on FAs and cell migration generally occur at much lower stiffnesses, between 0.2 and 100 kPa, and cell phenotypes generally plateau at levels comparable to those observed on glass, even below 100 kPa (DOI: 10.1242/jcs.133645, DOI: 10.1038/ncb3268, DOI:10.1039/c5ib00307e, DOI: 10.1039/c9sm01893j). Furthermore, substrate stiffness has much more moderate effects on confluent cells than on isolated cells. For example, it has been previously demonstrated that confluent layers of MCF10A epithelium showed no change in velocity coordination in the range of 3 to 65 kPa (DOI: 10.1083/jcb.201207148). Therefore, collagen-coated glass appears to be a reasonable model for the basement membrane. Overall, we believe that we have conducted our experiments under physiological conditions, and that our results apply to a wide range of substrate stiffnesses.

- It would be nice to see how long it takes confluent cell layers to close rectangular wounds of defined size when cells migrate as individual (adherens junctions perturbation) versus collective (wt) (on substrates of different stiffness). Presumably, there should be faster wound closure under the collective regime, at least for simple shaped wounds.

This is an interesting question, which our results indirectly address. In our study, we measured the wound healing speed of the WT MDCK cell line as well as lines expressing mutant vinculin constructs (Fig. 6A). These results show that this speed ranges from 5 to 15 µm/h depending on the construct expressed (and for reasons that we explain in the manuscript). These values make it easy to estimate the time required to close a wound based on its width. For example, it would take 5 hours to close a 100 µm wide wound for the WT cell line, which has a rate of 10 µm/h (on both sides of the wound).

Wound closure for cells with disrupted adhesive junctions has already been documented (DOI: 10.1083/jcb.200910041). The results show that wound closure is indeed slower than with WT cells. Although this previous study does not reveal the underlying causes, our work now shows that there are two factors: weaker directional memory due to impaired intercellular coordination and, in the longer term, an additional lack of sensitivity to the guidance signal provided by the wound.

- Akin to substrate stiffness variation, I am missing experiments that test the effect of cytoskeletal tension on these migration modes. Experiments with Rho kinase or myosin inhibitors could meaningfully broaden the scope of this study.

Rho kinase or myosin inhibitors applied to cells during the time required to assess migration patterns (a movie recorded overnight is necessary to obtain a statistically reliable calculation of MSD over 3 to 4 hours) are likely to affect many other cellular processes in addition to the cytoskeletal tension directly involved in migration. We believe that the accumulation of these effects will make interpretation of the results very difficult. For example, it has been shown that inhibition of ROCK by Y27 promotes healing of corneal endothelial lesions by affecting proliferation through cyclin D and p27 (DOI: 10.1167/iovs.13-12225), or by improving respiration, which would provide the energy necessary for migration (DOI: 10.1096/fj.202101442RR). Consistently, another study on HaCaT epidermal cells confirms that myosin phosphatase accelerates wound healing through proliferation (DOI: 10.1016/j.bbadis.2018.07.013). In contrast, in HUVEC cells, ROCK inhibition significantly impaired the proliferation and migration of vascular endothelial cells in vitro in a dose-dependent manner (DOI: 10.1097/ICO.0000000000000493).

Furthermore, previous studies have highlighted that differential contractility at the subcellular level is important for collective migration (DOI: 10.1038/ncb2133, DOI: 10.1083/jcb.201706013), which is not possible to examine with global activation or inhibition of contractility. This prompts the development of more refined and specific measurement and disruption strategies to assess the respective impact of cytoskeletal tension on cell-cell and cell-matrix adhesion mechanisms. Our work, which uses biosensors to assess how this tension differentially affects cell-cell and cell-matrix adhesions, is a step in this direction. The localized spatio-temporal activation or inhibition of myosin subtypes or Rho GTPase regulators specific to these adhesion structures will likely answer these questions in the future, but we believe that the development and application of these approaches will require a substantial amount of work that goes beyond the scope of our study.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

Summary:

The authors set out to investigate how well the onset of a self-initiated movement could be predicted at different times prior to action onset. To do so, they collected EEG and MEG data across 15 human participants who watched natural landscape images on a screen. These participants performed active self-initiated movements, or observed passive actions, to have a new image appear. By comparing the neural activity prior to active and time-matched passive actions, the authors found that even though a build-up of neural activity is visible close to 1s prior to action, action onset could only be reliably predicted around 100ms prior to action. These results confirm what was already suggested in previous literature: the commitment to action is only clear from the late stages in the visible neural ramp-up to action onset.

Strengths:

(1) The paper presents a well thought out methodology to assess the predictive value of neural activity prior to a self-initiated movement and passively observed action, while keeping all other experimental factors identical. This methodology can be applied outside the specific scope of this paper as well, in efforts to assess the correspondence of a neural signature with an observed behavior.

(2) The results are a strong confirmation of what was suggested less clearly in previous research (Trevena & Miller, 2010, Consciousness & Cognition; Schmidt et al., 2016, Neuroscience & Biobehavioral Reviews; Travers et al., 2020, NeuroImage).

Comments on revised version.

I thank the authors for addressing my concerns in the Introduction and Discussion of their paper. I don't require any further edits at this point.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Please more concretely define the parameters of 'early' and 'late' time windows in the manuscript so that the reader can better understand the difference between these with respect to the time-course of effects relative to a motor response.

Those changes were addressed in the previous round of revisions (please refer to previous round). Namely, we made the following addition:

“The lower bound of meta-analytic estimates of awareness, at 250 ms before movement onset (Braun et al., 2021), can be used as a pragmatic threshold to classify neural signals as “early” (more than 250 ms before movement onset) or “late” (less than 250 ms before movement onset).”

(2) Code and data do not appear to be uploaded to the linked OSF repository. We understand that this may typically occur after the reviewed preprint is available via eLife; however, please ensure that this is made publicly available. Because such materials were not available, we were unable to verify some of the method's details and went by what was reported in the preprint.

We apologize for the oversight, the link to the code was in the description of the OSF data repository that was linked in the data availability statement. We have now updated the data availability statement to directly reflect links to both the data (OSF) and the code (GitHub):

“Data used in this study are publicly available on the OSF repository: https://osf.io/wm95q/.

Code used in this study is publicly available on GitHub: https://github.com/lucasjeaybizot/Slideshow2025.”

(3) For the sentence: 'Proponents of the early-decision account have taken early brain activity, like the RP, to support the thesis that decisions happen early in the brain, taking these early signals to reflect a cascading process that brings about the forthcoming action.' it would be very informative to cite the papers that propose this account, as only the Schurger et al. (2021) paper is cited in this paragraph.

We have modified the sentence to the following to include the original result (Libet et al., 1983), an influential review that describes this interpretation (Haggard, 2008), and an influential study that applied such interpretation (Fried et al., 2011):

“Proponents of the early-decision account have taken early brain activity, like the RP, to support the thesis that decisions happen early in the brain, interpreting these early signals to reflect a cascading process that brings about the forthcoming action (Libet et al., 1983; Haggard, 2008; Fried et al., 2011).”

(4) In Figure 2C, the units are not displayed in the colour bar. These should be included so that the colours can be better interpreted.

The units have now been added to the figure.

(5) It is unclear why the time-frequency power estimates (and multiple comparisons procedures) extend to an upper limit of 80 Hz (as displayed in Figure 2C), despite the key signal of interest only spanning 10-30 Hz (Mu/Beta range). Extending the frequency range this high results in a larger number of comparisons and a potentially stricter multiple comparisons correction. Please justify why this larger frequency range was used, given this potential drawback.

The rationale for extending the time-frequency decomposition to 80 Hz was to characterize the spectral landscape over the same frequency range that was available to the Haar-AdaBoost classifier, whose features extended up to 80 Hz. The purpose of this analysis was therefore not limited to testing the canonical mu/beta ERD range, but also to visualize whether other frequency-specific activity was present in the broader feature space used by the classifier. We have clarified this rationale in the text:

“We examined this broader frequency range, rather than restricting the analysis to the canonical Mu/Beta bands, to characterize the time-frequency landscape over approximately the same spectral range available to the Haar-AdaBoost classifier, whose frequency-sensitive features extended from 2 to 80 Hz.”

(6) For the time-frequency analysis, it is stated that 'Here, we used complex Morlet wavelets to decompose our data at C3 into 78 logarithmically spaced frequency bands from 2 Hz to 80 Hz with logarithmically decreasing cycle counts'. Do the authors mean logarithmically increasing in this case? Usually, more cycles are used for higher frequencies to achieve a similar time/frequency precision balance across lower and higher frequency wavelets. Fewer cycles for higher frequencies is highly unusual. This should be corrected if it is an error.

We thank the reviewer for catching this important error. We indeed used an increasing cycle count. We have modified the text accordingly by changing the description to “increasing”.

(7) Regarding the sentence: 'We used standard procedures for identifying and interpolating bad channels in the EEG recordings.' Please specify what those procedures are, as they are not necessarily standard across different research groups, and multiple methods exist.

We have modified the section to better describe the procedures:

“We manually identified bad channels and interpolated them using a weighted average of the 5 nearest channels.”

(8) For the ERP analyses of differences between the active and passive conditions, the parameters of the cluster-based permutation test should be specified (e.g., the alpha levels for cluster inclusion and cluster-level statistical significance).

We have added the following to better characterize the cluster-correction parameters:

“Samples exceeding a two-sided uncorrected threshold of were grouped into temporal clusters, and the cluster statistic was defined as the sumα of = 𝑡.-05 values within each cluster. Statistical significance was assessed using 1,000 permutations, with clusters considered α =. 05 significant at a cluster-level based on the two-sided permutation distribution.”

Reviewer #2 (Recommendations for the authors):

(1) I am curious how the current results would compare to an analysis in which pre-action neural activity is compared to baseline and post-action neural activity. In other words, activity at any point in time during which the person was at rest, rather than an explicit time-matched passive action condition. I would expect that neural activity predictive of an upcoming action or intention will look significantly different from the neural activity in time at any other moment at which the person is not intending to act.

We agree that comparing pre-action activity with unconstrained resting activity could be informative and would likely reveal differences associated with preparation for action. However, this comparison would address a somewhat different question from the one targeted here. Our goal was to determine whether activity preceding self-initiated movement contains information specific to the forthcoming movement when compared with a temporally matched condition that controls for elapsed time and anticipation of the slide transition. An arbitrary resting baseline would not provide these controls and could therefore introduce differences unrelated to movement commitment. We agree that such an analysis could be useful in future work.

(2) It would be good to discuss the current results in comparison with those of Trevena & Miller (2010, Consciousness & Cognition).

We have addressed this comment in the previous round of revision:

“Previous work showed that these early ramping signals were not specific to the outcome of a motor decision (Trevena & Miller, 2010). However, because their analyses remained time-locked to decision outcomes, they could not directly test whether the observed slow buildup specifically reflected a commitment-like process.”

(3) The order of reporting throughout the paper is somewhat confusing, as many results are provided before the "Results" section. For example, there is repetition in the "A new approach to self-initiated movement analysis" section, compared to the "Results" section. The argument for why event-locked potentials are not necessarily predictive in value is also repeated multiple times throughout the paper. The paper could benefit from some restructuring to avoid repetition.

We appreciate this point. Some repetition is intentional because the Introduction motivates the methodological problem and previews the logic of the analyses before the formal Results section. We deem this contextual overlap necessary for adequately understanding the rationale for the study at each stage of the manuscript, we have therefore retained the current overall structure.

(4) Is there a particular reason why this paper includes and compares both EEG and MEG data?

The earlier held-out dataset collected at PF included both EEG and MEG, whereas the independent main dataset collected at OC used EEG only. We used the PF EEG data for model selection and parameterization, while the independent OC EEG dataset served as our main test set. Showing that the same overall pattern was present across EEG and MEG also provided an opportunity to assess whether the result generalized across recording modalities.

(5) Is there a particular reason why the AdaBoost results are compared to the outcome of an SVM and Random Forest?

We compared AdaBoost with SVM and Random Forest as part of the model-selection procedure on the held-out PF dataset. Each algorithm was evaluated with a range of feature representations, and Haar-AdaBoost produced the highest AUC in the window immediately preceding slide transition. It was therefore selected for the primary analyses. We additionally compared Haar-AdaBoost post hoc with several standard EEG classifiers, including CSP-LDA and EEGNet, to assess whether the main temporal pattern depended on classifier choice. This supports our claim that lack of early classification is due to non-separability of the data rather than classifier selection.

Author response:

We thank the editors and reviewers for their careful and constructive evaluation of our manuscript. We are encouraged that the reviewers recognize the value of our biochemical, biophysical, structural-modeling, and cell-based analyses of kinesin-1 holoenzyme assembly, KHC–TRAK2 recognition, and the regulatory interplay between KLC1 and TRAK2. We also appreciate the concerns regarding the relationship of our findings to previous work, the strength of several mechanistic conclusions, validation and presentation of the structural models, and the need for additional controls and quantitative analyses.

We plan to revise the manuscript substantially in response to these comments. Our provisional responses and planned revisions are summarized below.

Reviewer #1

We agree that the novelty of several findings should be more carefully defined in the context of the existing literature. In the revised manuscript, we will better integrate previous biochemical and structural studies of KHC–KLC assembly, TRAK-family adaptor binding to KHC, and kinesin-1 autoinhibition. In particular, we will explicitly compare our findings with the work of Diefenbach et al. [1]., Weijman et al. [2]., Tan et al. [3]., Ashaduzzaman et al. [4]., and Gladkova et al. [5]., and distinguish previously established structural features from the additional residue-level mutational validation and quantitative biophysical analyses provided in our study. We will accordingly revise statements of novelty throughout the manuscript.

We also agree that our current data establish a direct CC1–CC4 interaction and its disruption by TRAK2 and KLC1, but do not directly demonstrate that this interaction is itself autoinhibitory or that its disruption activates full-length kinesin-1. We will therefore distinguish the experimentally observed CC1–CC4 interaction from the proposed regulatory model and temper terms such as “autoinhibitory latch,” “activation switch,” and related mechanistic conclusions where appropriate. We will also expand the Discussion to consider how this interaction may relate to the established roles of full-length KLC and MAP7 in kinesin-1 regulation.

To strengthen the presentation of the AlphaFold3-based models, we will provide model-confidence information, including pLDDT, PAE, and ipTM metrics, specify the exact sequences and residue boundaries used for each prediction, and include additional prediction outputs where informative. We will also more clearly distinguish experimentally supported conclusions from structural hypotheses, particularly regarding the proposed steric and/or conformational effects of the extended KLC1 coiled-coil on the KIF5C CC4 region.

Finally, we will strengthen the quantitative and methodological presentation of the study. We will provide clearer construct information, explicitly report experimental replication, quantify the mitochondrial enrichment and cellular distribution analyses in Figures 4 and 5, and revisit the interpretation of stoichiometries obtained with shorter coiled-coil fragments. Statements implying mitochondrial transport will be revised to reflect that the current cellular experiments directly demonstrate mitochondrial recruitment rather than organelle motility.

Reviewer #2

We agree that the relationship between our study and previous structural work should be made substantially clearer. Although several relevant studies were cited in the original manuscript, the extent to which our findings confirm, extend, or differ from these previous models was not sufficiently explained. We will revise the Introduction, Results, and Discussion accordingly, including explicit comparisons with the structural predictions of Weijman et al. [2]., the XL-MS-supported model of Tan et al. [3]., the recent cryo-EM/integrative model of Ashaduzzaman et al. [4]., and the TRAK–KHC work of Gladkova et al [5].

We also appreciate the concern that mutations introduced into hydrophobic interfaces could affect the intrinsic stability or homodimerization of KHC or TRAK2, rather than selectively disrupting heterotypic interactions. To address this alternative explanation, we plan to evaluate the oligomeric states and stability of key interface mutants using appropriate biophysical approaches, including SEC-MALS and thermal-stability measurements. These results will be incorporated into the revised manuscript and used to reassess the interpretation of the corresponding binding and cellular recruitment experiments.

As noted above, we will also provide substantially more information on the confidence and reproducibility of the AlphaFold3 predictions, including pLDDT, PAE, and ipTM metrics, and will clearly annotate the residue boundaries of all modeled fragments.

Reviewer #3

We agree that the cellular experiments require additional quantification and clearer presentation. We will quantify the mitochondrial enrichment of KIF5C and the effects of KLC1 co-expression on the intracellular distribution of KIF5C and TRAK2 across independent experiments. We will also include appropriate controls for endogenous/background fluorescence, improve image and scale-bar presentation, and revise the corresponding terminology so that the conclusions accurately reflect the experiments performed.

We will strengthen the reproducibility and presentation of the biochemical and biophysical data. Key ITC measurements will be supported by independent repeats and reported with the corresponding binding parameters and variability. For the SEC experiments in Figure 3, we will include SDS-PAGE analysis of relevant fractions and more clearly describe the composition of each protein mixture. Appropriate positive controls will also be added to the Co-IP experiments where requested.

We will further improve the presentation of the structural models by providing confidence metrics and residue annotations, and we will carefully revise the terminology used to describe SEC, SEC-MALS, ITC, and other biochemical approaches. The Abstract and main text will also be edited to more clearly describe the experimental approaches used and to ensure that all mechanistic conclusions are matched to the strength of the available evidence. More broadly, we will revise the manuscript to sharpen its central message while avoiding overstatement. In particular, we will distinguish direct experimental observations—such as KHC–KLC1 assembly, KHC–TRAK2 recognition, KLC1-dependent modulation of TRAK2 engagement, and the CC1–CC4 interaction—from mechanistic models that remain to be tested more directly.

We expect to complete these revisions and associated experiments within approximately 10–12 weeks. We thank the editors and reviewers again for their constructive comments, which we believe will substantially improve the rigor, clarity, and positioning of the study.

(1) Diefenbach RJ, Mackay JP, Armati PJ, Cunningham AL. The C-terminal region of the stalk domain of ubiquitous human kinesin heavy chain contains the binding site for kinesin light chain. Biochemistry. 1998 Nov 24;37(47):16663-70. doi: 10.1021/bi981163r.

(2) Weijman JF, Yadav SKN, Surridge KJ, Cross JA, Borucu U, Mantell J, Woolfson DN, Schaffitzel C, Dodding MP. Molecular architecture of the autoinhibited kinesin-1 lambda particle. Sci Adv. 2022 Sep 16;8(37):eabp9660. doi: 10.1126/sciadv.abp9660.

(3) Tan Z, Yue Y, Leprevost F, Haynes S, Basrur V, Nesvizhskii AI, Verhey KJ, Cianfrocco MA. Autoinhibited kinesin-1 adopts a hierarchical folding pattern. Elife. 2023 Nov 1;12:RP86776. doi: 10.7554/eLife.86776.

(4) Ashaduzzaman M, Tang Y, Okada K, Fried SD, Mckenney RJ, Al-Bassam J. Structural basis of kinesin-1 autoinhibition and its control of microtubule-based motility. Sci Adv. 2026 Jul 17;12(29):eaeg1267. doi: 10.1126/sciadv.aeg1267.

(5) Gladkova C, Paez-Segala MG, Grant WP, Kittisopikul M, Myers SA, Wang Y, Vale RD. A molecular switch for coordinating kinesin and dynein transport of mitochondrial cargo. Science. 2026 Aug 6;393(6811):601-606. doi: 10.1126/science.aeh1475.

Author response:

We thank the reviewers for the overall positive review that declares our results convincing. We will revise the paper to improve the presentation of the model and results as suggested by the reviewers. The revision will be accompanied by a more detailed response.

Author response:

Reviewer #1 (Public review):

(1) The authors investigate the use of the knocked-in human immunoglobulin genes in heavy chains and light chains and provide the frequency of productive rearrangements using these genes. However, there is no information about the frequency of the right heavy-light chain pairs. This information would be important to calculate the real frequencies of potential bNAb precursors in these mouse models.

We acknowledge that our bulk sequencing-based repertoire analysis does not assess the pairing of immunoglobulin (Ig) heavy and light chains. To add this information, we plan to sort IgM⁺IgD^hi naive B cells from the mouse models and use single-cell RT-PCR to analyze paired heavy and light chains from individual B cells. Since the assay detects Ig transcripts, it will also address comment #2 about the lack of expression data for the human Ig segments.

The main goal of the single-cell RT-PCR experiment is to verify that the human Ig segments in the mouse models can be expressed as B cell receptors (BCRs) in naive B cells. However, because of its low-throughput nature, the assay is unlikely to be sensitive enough for detecting bnAb precursors. As shown in Figure 5G, the frequencies of bnAb-like CDR H3s for DH270, BG18 and PCT64 are in the range of 10^-4. The frequencies of paired bnAb-like heavy and light chains will be even lower. It will be difficult to robustly measure the frequencies of such rare BCRs even with 10x Genomic single-cell sequencing. For reference, 10x Genomic sequencing of B cells from 10E8 KI mice yielded 1026 heavy and light chain pairs (1). The sample size was adequate for analyzing light chains paired with the pre-rearranged 10E8 heavy chain, which is expressed in most B cells. The sequencing depth will be insufficient for detecting rare bnAb precursors in the rearranging mouse models of this study. Deep bulk sequencing data were used to calculate bnAb precursor frequencies in our previous VRC01 mouse models and in humans and nonhuman primates (2-8). It is possible to enrich bnAb precursors for single-cell analysis by sorting epitope-specific B cells (9-11). However, this method requires sorting probes that exhibit high affinity and selectivity for bnAb precursors. We believe immunization of the mouse models will be the most direct and definitive way to detect bnAb precursors and test their functions in these mouse models. As mentioned in the manuscript, we have already provided the mouse models to several investigators for immunization experiments.

(2) The authors use HTGTS-rep-seq to investigate immunoglobulin gene rearrangements at the genomic DNA level. This method is very useful for analyzing gene recombination because it provides information about both productive and non-productive rearrangements. However, this method does not provide information about BCR expression, and it is not optimal for investigating repertoire composition. BCR expression would provide a more rigorous characterization of the mice and confirm functionality.

It is true that HTGTS-rep-seq does not directly show the expression of productive rearrangements. As outlined in our response to comment #1, we plan to perform single-cell RT-PCR to confirm the expression of the integrated human Ig segments in IgM⁺IgD^hi B cells.

We have used HTGTS-rep-seq extensively to analyze V(D)J rearrangements. Overall, the outcomes of the repertoire analysis correlated well with functional assays of BCR expression. For example, we identified VRC01-class heavy and light chains in VRC01 mouse models with HTGTS-rep-seq; correspondingly, immunization of the mouse models elicited VRC01-class antibodies (7, 8, 10). As another example, we used HTGTS-rep-seq to characterize V(D)J rearrangements at different stages of B cell development (12). The ratio of productive/nonproductive V(D)J rearrangements increases as B cells mature. The correlation suggests that the productive rearrangements, as detected by HTGTS-rep-seq, are selected by virtue of their expression as BCRs, which are required for B cell maturation and survival.

(3) The goal of this study was to produce models that could provide a diverse bNAb-like repertoire. Specific quantification of the diversity of the repertoire is not provided. The study does not provide information about the sequences that do not use the intended genes.

In our previous analysis of the VRC01 mouse models, we calculated the proportion of unique CDR3s and CDR3 overlap among different animals and used these parameters to represent repertoire diversity (7, 8). We will perform the same analysis for the six mouse models in this study. The V(D)J rearrangements that do not use the human Ig segments are composed of mouse Ig segments, and we will show repertoire analysis of these rearrangements in the revised manuscript.

Reviewer #2 (Public review):

(1) Abstract Clarity:

Concluding sentences should incorporate the discussion's explanation: finding natively low-frequency precursors in standard humanized locus mice is statistically prohibitive due to their smaller absolute B-cell compartment. These models bypass this restriction by maximizing relevant segment expression to expand the functional CDR3 search space.

We will make the suggested change in Abstract.

(2) Results (Line 183, BG18 expansion):

The intriguing expanded B1 cell population warrants more conservative commentary regarding genuine autoreactivity versus other possibilities, such as hyperactive baseline signaling via autophosphorylation (as shown by Hassan Jumaa for certain HC/LC clonotypes). While beyond this manuscript's scope, these mechanisms are differentiable via calcium flux assays with general anti-BCR signaling reagents.

We are currently examining the cause of B1 cell expansion in the BG18 model. Our preliminary data suggest that some of the B1 cells express autoreactive antibodies, but more work is needed to reach a conclusion. Until then, we are open to alternative possibilities, as suggested.

(3) Results (p15/Line 324, PCT64/CH235 Vκ Allelic Architecture):

The text states that lacking a recombination cassette caused hVκ3-20 to account for only a fraction of rearrangements. While Figure 1B's general engineering feature (tandem reverse hJκ-RSS 23 and 12 RSS hJκ) implies human Vκ should predominate everywhere, Figure 1C suggests hVκ3-20's low representation in CH235 and PCT64 models stems from being introduced differently-specifically via pre-rearranged minigenes rather than unaltered RSS orientations in an unrearranged cassette. The authors should clarify this point in the text and/or Figure 1.

The recombination cassette, as diagrammed in Figure 1B, is not in the CH235 and PCT64 models. Instead, the hVk3-20 allele in these models was derived from one of the previous VRC01 mouse models (7). As described in the Luo et al paper (7), hVk3-20 replaces mouse Vk3-7 in the Igk locus, but all the other mouse Vk segments are intact and functional. In this configuration, hVk3-20 rearranges as one of the Vk segments in Igk allele and accounts for about 10% of total Igk rearrangements. We will clarify this point in the revision.

(4) Results (p14, Clever Engineering of λLC rearranging mice):

Replacing mCκ with hCλ3 is a clever genetic trick and an important proof of concept for stably accommodating a human lambda rearranging light chain cassette within the mouse kappa locus. This excellent methodological highlight deserves prominent recognition as a template for other model developers. I suggest giving this further play in the discussion.

We will highlight this design in the discussion.

(5) Discussion (Model Comparisons & Baseline Resolution):

The authors aptly compare these humanized mice to macaques; in addition to their superior scalability, they point out that macaques don't recapitulate human-specific bnAb-relevant configurations in certain instances (like lacking the VH1-2 minigene for VRC01-class responses, or utilizing germline D segments that favor V2 apex responses, potentially overestimating human responses). To further enhance nuance, referencing other prior review KI model literature on this topic (some published by these authors) would be beneficial. For context, KI-derived adoptive transfer models offer more potential diversity (thus, 'higher bar' off-target response testing) and frequency control but are restricted to short priming studies. Conversely, the rearranging models in this study support full vaccine regimens and generate multiple variant bnAb precursors to compare potential in vivo response plasticity.

As suggested, we will include additional references and comparisons of the Ig humanized mouse models with KI mice. The reviewer raised an important point about off-target responses. Adoptive transfer models have the full mouse antibody repertoire. By comparison, the antibody repertoires of the Ig-humanized mouse models are dominated by a select set of human Ig segments, with minimal contribution from mouse antibodies. From this perspective, the adoptive transfer model provides a more diverse range of potential off-target antibodies. On the other hand, the Ig-humanized mouse models may be superior to wild-type mice in producing antibodies against the immunogenic glycan holes in envelopes (13). Reaching these glycan holes may require sufficient CDR H3 length, and based on CDR H3 length distribution, Ig-humanized mouse models could be more capable of recapitulating this type of off-target response than wild-type mice.

(6) Discussion (Baseline phenotypes):

One limitation of the cellular flow data, albeit beyond the manuscript's current scope, is that the baseline phenotypes predominantly reflect variations of a fixed pair of V(D)J rearrangements, rather than bona fide patient-derived UCA bnAb precursors with correct charges/lengths. To help resolve pre-antigenic functional signaling boundaries and thus potentially aid immunogen design, the discussion could note how future work could aim to use techniques like single-cell transcriptomics to map expressed selection signatures of bnAb precursor paired V(D)J's to rule out anergy or survival/death gene signatures.

The reviewer is correct that the surface phenotypes of rare bnAb precursor B cells, such as low BCR levels on anergic B cells, may not be apparent in the bulk flow cytometric analysis. Single-cell transcription signature analysis would be a high-resolution method to analyze bnAb precursor B cells. The technical challenge is low bnAb precursor frequencies, and enrichment of bnAb precursors by immunogen sorting may be the necessary for their detection. We will discuss this point in the revised manuscript.

(7) Discussion (PG9 Model & HCDR3 Length Constraints):

While the PG9 model's failure to produce bona fide precursors is unsurprising given its long HCDR3, the authors should provide a bit more detail as to whether a subset of PG9 variants with slightly shorter HCDR3s are permissive for bnAb production (analogous to DH511/10E8). Providing the specific HCDR3 sizes generated by this model in relation to recently discovered monkey antibodies-which are shorter/different but function like PG9 bnAbs (e.g., Guenega et al Nature 2026) - would offer excellent context. Such related lineage and/or lineage precursor variants could serve as structural alternatives, and highlighting how these length constraints impact selection provides vital boundary conditions for the immunogen design field when planning germline-targeting regimens.

The suggested recent studies (14-17) showed that V2 apex targeting is achievable with relatively shorter CDR H3s (22-25aa), which are within reach in the PG9 mouse model. However, the rhesus antibodies utilize IGHD3-15 with optimal V2 apex targeting motif. It remains to be determined whether hD3-3-based antibodies with comparable CDR H3 length would function similarly. We will incorporate the new information from rhesus immunization studies into the discussion.

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(13) McCoy LE, van Gils MJ, Ozorowski G, Messmer T, Briney B, Voss JE, et al. Holes in the Glycan Shield of the Native HIV Envelope Are a Target of Trimer-Elicited Neutralizing Antibodies. Cell Rep. 2016;16(9):2327-38.

(14) Marchitto L, Wagh K, Roark RS, Coleon S, Li H, Skelly AN, et al. Enhanced B cell priming induces broadly neutralizing HIV-1 apex antibodies. Nature. 2026;656(8128):712-22.

(15) Guenaga J, Ádori M, Bale S, Phulera S, Zygouras I, Schleich FA, et al. Vaccination generates broadly cross-neutralizing antibodies to the HIV Env apex. Nature. 2026;654(8119):777-85.

(16) Mishra N, Liang B, Roark RS, Ghosh AR, Callaghan S, Lee WH, et al. Germline-targeting HIV immunogen induces cross-neutralizing antibodies in outbred macaques. Immunity. 2026;59(4):1140-60.e11.

(17) Ma KM, Sutton HJ, Pratap PP, Steichen JM, Carnathan D, Quinn J, et al. HIV broadly neutralizing antibody precursors to the Apex epitope induced in nonhuman primates. Sci Immunol. 2025;10(110):eadt6660.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study by Damphousse, Calvin, and Redish investigates how the hippocampus represents competing future outcomes during approach-avoidance conflict. Using an ethologically relevant robotic predator foraging paradigm, the authors aimed to dissociate hippocampal activity associated with reactive defensive responses (escape) from that linked to anticipatory withdrawal decisions. The central finding is that dorsal hippocampal representations differentiate these two modes of defensive behavior within a single naturalistic assay. Specifically, the authors show that attack-triggered retreats and mid-track aborts differ in movement dynamics and hippocampal spatial decoding despite sharing a common behavioral endpoint, that hippocampal representations during pauses predict subsequent behavioral outcomes, and that these representational biases emerge before overt behavioral divergence. The main importance of the study lies in moving beyond viewing the hippocampus as merely encoding spatial location or threat salience, instead suggesting that hippocampal ensemble activity dynamically tracks and differentially weights threat-related, reward-related, and safety-oriented future states to bias behavior before overt action occurs.

Strengths:

The study has several notable strengths. First, the behavioral decomposition into retreats, mid-track aborts, and mid-track continues is rigorous and provides a highly interpretable analytical framework. Second, replication across two independent cohorts - despite differences in arena configuration, robot design, and extinction procedures - meaningfully strengthens confidence in the robustness of the findings. Third, the unified reanalysis pipeline across cohorts reflects strong analytical discipline, and the Bayesian decoding framework is well-suited to addressing the central representational questions. Fourth, the ethological relevance of the robotic predator paradigm is a major advantage, allowing the authors to examine a richer repertoire of defensive and decision-related behaviors than is possible in conventional fear-conditioning assays. Overall, the experiments are well designed, the data are clearly presented, and the findings make a valuable contribution to understanding how the hippocampus supports decision-making under threat.

Weaknesses:

The study is technically strong, but a few modest revisions would further enhance it.

(1) First, the abstract mentions extinction and reinstatement effects, but neural analyses focus primarily on the attack phase. It would be helpful to clarify or adjust the abstract accordingly.

(2) Second, some interpretive language ("guide," "bias") leans toward causal phrasing. Given the correlational data, using "predict" or "correlate with" would be more precise.

(3) Third, given the relationship between running speed and hippocampal theta, considering speed-related contributions to decoding differences would be useful.

(4) Fourth, reporting turnaround positions for mid-track abort and continue trials (Figure 7) would provide helpful context.

(5) Fifth, a figure comparing stimulated vs. non-stimulated sessions in cohort 2 would support the claim that closed-loop stimulation had no measurable effect.

(6) Finally, reporting effect sizes for key decoding comparisons would add clarity.

Reviewer #2 (Public review):

Summary:

This manuscript extends previous work from Calvin et al. and examines hippocampal representations during approach-avoidance conflict in a robotic predator foraging task. The paradigm itself is very interesting and addresses an important but relatively understudied question in the navigation and foraging literature: how the brain balances risk versus reward during goal-directed behavior. While hippocampal representations of positively valenced goals and future intentions have been extensively studied, much less is known about how these representations evolve during risk-reward tradeoffs involving threat.

The authors use a relatively simple and interpretable decoding approach together with thoughtful behavioral comparisons to ask whether future behavioral outcomes can be read out from hippocampal activity before behavior diverges. The most compelling comparison is between mid-track aborts (MTAs) and mid-track continues (MTCs), where the animals initially exhibit very similar pause behavior but ultimately either abort or continue the trajectory. The authors show that decoded location during these pauses differs prior to the overt manifestation of the behavioral decision, suggesting that hippocampal representations may reflect evolving internal evaluation processes during approach-avoidance conflict.

Strengths:

A major strength of the work is the behavioral paradigm itself. This type of risk-reward conflict task is relatively uncommon in the hippocampal navigation literature and provides a rich framework for examining defensive decision-making during naturalistic foraging behavior.

The decoding analyses are also relatively simple and easy to interpret. Rather than relying on highly complex modeling approaches, the authors use straightforward comparisons of decoded spatial representations across behavioral conditions, making the results accessible and conceptually clear.

Another strength is the use of behavioral controls to isolate comparisons between related behaviors. In particular, the comparison between MTAs and MTCs is compelling because the animals exhibit similar pause states before the behavioral outcomes diverge. This provides a useful framework for asking whether hippocampal activity reflects future behavioral outcome before the decision is overtly expressed.

Overall, the study asks an interesting question using a novel paradigm and provides evidence that hippocampal representations during approach-avoidance conflict may reflect future behavioral trajectory.

Weaknesses:

The main weakness is that many of the reported effects are relatively subtle and are not sufficiently controlled for differences in speed, trajectory structure, and other behavioral variables across conditions. While the subtraction plots (green versus purple decoding differences) appear visually striking, the actual effect sizes are fairly small, making it difficult to assess how robust or behaviorally meaningful these differences are.

Relatedly, many of the most interesting questions in this task concern how behavior unfolds dynamically within a trial, yet much of the analysis averages across events and trajectories. As a result, potentially important aspects of the behavior may be obscured.

In particular, the manuscript would benefit from richer characterization of the animals' actual movement trajectories and spatial strategies. Because the analyses rely heavily on linearized position, it is difficult to determine whether animals behave differently in two-dimensional space across conditions. For example, during continued approaches, do animals preferentially hug the wall opposite the robot? Do different behavioral conditions show distinct lateral occupancy or trajectory structure? These types of analyses would make the behavioral interpretation substantially more compelling.

More generally, while the results are suggestive and interesting, the relatively small decoding differences and substantial behavioral confounds make it difficult to conclude that the observed effects reflect distinct internal evaluative or threat-related states.

Reviewer #3 (Public review):

Summary:

The study reanalyzes data from a previously published cohort together with an additional cohort to investigate hippocampal activity during approach-avoidance conflict. Unlike many prior studies that isolate reward- or threat-based learning, this task requires animals to evaluate reward and threat concurrently. The central finding is that hippocampal representations differ between hesitant behaviors that lead to approach versus avoidance outcomes, with representations of the attack zone more likely during pauses preceding abort decisions. This is an important extension of prior work on hippocampal activity and deliberation, suggesting that the hippocampal content may help shape the eventual outcome.

Strengths:

All behavioral findings are replicated independently across cohorts, making the behavioral results highly convincing. The design is robust, and the task is especially valuable for studying approach-avoidance conflict. The behavioral paradigm is complex and rare, and neuronal recordings in such a paradigm are of great value.

The major strength of the study is the comparison of neural activity during hesitant behavior leading to different outcomes, namely, pauses followed by the animal aborting the approach (mid-track aborts), and pauses followed by the animal committing to the approach (mid-track continues). Hippocampal activity differed between the two pauses: the attack zone was more likely to be represented during mid-track aborts. The same effect was observed on the journey before the pause: even before the animal hesitates, hippocampal activity before a pause that led to a mid-track abort was more likely to represent the attack zone than hippocampal activity before pauses that led to continued approach. This analysis suggests that hippocampal content before and during deliberative behavior is predictive of the animal's decision.

Weaknesses:

The interpretation of the retreat-related decoding results is less clear. The study compares two sets of retreating behavior: on the one hand, retreat after being attacked, and on the other hand, retreat after hesitation in the absence of an attack (a mid-track abort). Hippocampal activity represents the attack zone more after the animal is attacked. However, these two retreating behaviors originate from different spatial locations: retreats always start past the "attack threshold", while mid-track aborts always start before this threshold. Given that hippocampal decoding is strongly location-dependent, this difference in position makes the neural decoding results difficult to interpret. The increased representation may be due to differences in physical location, rather than the distinct processing of immediate threat and an anticipatory return state.

We thank the reviewers for their careful, constructive, and fair assessment of our manuscript, “Hippocampal representations differentiate reactive and anticipatory responses during foraging under threat.” We were pleased that the assessment characterized our study as important and the evidence supporting its main finding as solid. We also appreciate the reviewers’ recognition of the strengths of the behavioral paradigm and the conceptual contribution of distinguishing hippocampal representations associated with reactive and anticipatory responses to threat.

We carefully considered the reviewers’ comments and do not feel that the manuscript requires extensive revision. The reviewers suggested several thoughtful additional analyses, including further behavioral controls and explicit predictive analyses. We agree that these would be informative and intend to carry several of these directions forward with future datasets. However, for the present manuscript, the suggested analyses would extend the scope of the work but are unlikely to substantially alter the central observations, and we have therefore chosen not to undertake them for the present manuscript.

We have only made very minor changes to the text and figures, corresponding to what we might do in a manuscript that had been “accepted” under the old-style journal process. We have

- Revised the abstract to more accurately reflect the neural analyses presented.

- Softened the interpretive language throughout to avoid implying causality where the data establish associations, and explicitly acknowledged this limitation in the discussion.

- Clarified the explanation of the timing and location of robot attacks relative to the attack threshold.

- Clarified the definitions and explanations of the temporal segmentation of MTA and MTC pauses.

- Clarified the explanations of the outbound epoch used in the MTA-MTC comparison.

- Expanded the methods describing temporal and spatial normalization of behavioral epochs.

- Moved the headers on figures 5-7 as suggested by the reviewers to make them more clear.

With these revisions, we believe the manuscript now accurately reflects what can be concluded from the current data and appropriately acknowledges the limitations raised during review.

We sincerely thank the editor and reviewers for their thoughtful engagement. Their comments have improved the clarity and precision of the manuscript and provided valuable directions for future work.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

There are no major concerns, but some material could be added for clarity and to make the work more accessible to a more general scientific audience.

We will add text for clarity and to make the work more accessible to a general audience per this comment and similar suggestions of the other reviewers.

(1.1) A figure clearly showing the habituation protocol and the use of the dishabituators would be a good addition, even if the procedure has been done before and is cited. There can always be readers who are seeing this for the first time.

We do think this is a good idea as the time scales of the experiment will be clearly marked as well and we plan to generate one in the revised manuscript.

(1.2) It would also be nice to comment on other ways dishabituation can happen (for example, when the stimulus is removed for a short time and returns) and what their time scales are.

If the stimulus is withheld, spontaneous recovery occurs, a process distinct from dishabituation and worth exploring on its own. In a previous publication (Semelidou et al. eLife 2018;7:e39569), we have shown that in this habituation paradigm with 4 min exposure either to the aversive Octanol, or the attractive Ethyl Acetate, spontaneous recovery occurs on or after 6 minutes after the habituated stimulus is withheld. This contrasts the immediate effect of the single dishabituating stimulus, delivered for a few seconds at the end of exposure to the habituator. Granted that per Thomson (Neurobiol Learn Mem. 2009), spontaneous recovery is a characteristic of habituation, we will work this point in the text.

(1.3) And more generally, the paper could perhaps improve by making a stronger case for why the results are important not just for flies but for neuroscience in general.

Thank you for the encouragement. We will try to rationally generalize our findings.

Reviewer #2 (Public review):

(2.1) However, the claim that this represents a fundamental difference between homosensory and heterosensory pathways for dishabituation is overstated.

We had no intention of stating more than the fact that footshock and yeast odor dishabituators relay these stimuli to the mushroom bodies via distinct dopaminergic neurons, hence differentiating distinct dishabituating stimuli via the mechanosensory (footshock) and olfactory (yeast odor) modalities as they engage the mushroom bodies. As the reviewer suggests we will use more measured and specific language to state the above.

(2.2) The introductory section does not adequately present current broad models for habituation and dishabituation.

This was not done intentionally, but rather because we aimed at a less extended introductory section and ostensibly this resulted in brief and possibly inadequate presentation of current habituation models. We will present a much more detailed introduction and detail of habituation and dishabituation models in the revised manuscript (Also see reply to point 3.5 below).

(2.3) There are many different time scales, even for Drosophila olfactory habituation. These, as well as potential underlying mechanistic differences, need to be acknowledged; any claim should be specifically qualified for the time scales being studied here.

We understand and appreciate the point of the reviewer, as well as its significance and we will address this both in the revised text, but also by the paradigm figure we will add as stated above (point 1.1), where the time scales will be explicitly included and emphasized.

(2.4) Additionally, there are several unclear, vague, and inaccurate sections and statements. A more careful, precise, and considered presentation of current views, as well as more measured claims of the impact of the findings, would substantially enhance my enthusiasm.

We will address these concerns of course, though pointing out the specific offending parts would ascertain addressing them thoroughly. As stated above, we will incorporate current views in the introduction and when discussing our results and their impact.

Reviewer #3 (Public review):

(3.1) The key issue is that the main concepts of this manuscript appear to be based on a misunderstanding/misinterpretation of the literature. As the authors set out to settle the debate "whether the novel dishabituating stimulus elicits sensitization of the habituated circuits, or it engages distinct neuronal routes to bypass habituation reinstating the naïve response", it seems that the authors based their investigation on the premise that "sensitization" is mediated by a facilitatory process within the S-R pathway, and "dishabituation" by a facilitatory process outside the S-R pathway. This is not the status quo in the field, particularly with the prevailing theory like the Dual-Process Theory.

We appreciate the reviewer’s comment and the opportunity to clarify the conceptual framework of our work. Our intention was in fact to test the Groves and Thomson hypothesis (Neurobiol Learn Mem. 2009), in our olfactory habituation system. As such, dishabituation could have been the result of a facilitatory process within the S-R pathway, or from mechanisms outside of it. Our experimental design allowed to distinguish these possibilities and our results clearly show that dishabituation involves circuitry outside the S-R pathway. We do thank the reviewer for pointing out that we have not articulated clearly this intention and we will take care to communicate this effectively in the revised manuscript.

(3.2) The original version of Dual-Process Theory (Groves and Thompson 1970, but also see Thompson 2008, Neurobiol Learn Mem) already hypothesized that habituation happens within the specific S-R pathway, and sensitization occurs separately in an "organism-wide" state system that modulates the output of all S-R pathways.

As mentioned above, we are aware of the Dual-Process hypothesis. In fact, our data demonstrate that activity outside the olfactory S-R pathway, engaging novel neuronal circuits, mediates dishabituation. Unlike habituation, these circuits mediating dishabituation include at minimum, the mushroom bodies, the dopaminergic system and the APL neurons. In our view this does not support the “organism-wide state” system, but rather particular circuits that in agreement with the Groves and Thomson hypothesis, are outside the S-R pathway and modulate its behavioral output. We will work these concepts in the discussion section of the revised manuscript.

(3.3) Dishabituation is recognized by the Dual-Process Theory as sensitization (organism-wide facilitation) manifested on top of existing habituation (depressed S-R pathway). This notion has been supported by a wide range of studies, including cat spinal cord reflex (e.g. Spencer et al. 1966) and work in Aplysia on heterosynaptic facilitation for both sensitization and dishabituation. Therefore, simply showing that the newly identified facilitatory pathways are outside the S-R habituation pathway is insufficient to demonstrate dishabituation.

We respectfully disagree with the concluding sentence here. In all of our experiments, we observe a clear recovery of olfactory avoidance after exposure to the footchock, or yeast odor dishabituators. Moreover, the dishabituators are emulated by (photo)activation of particular neuronal circuits and the recovery of olfactory avoidance is blocked when these circuits are silenced. Regardless of whether this recovery is classified as dishabituation via sensitization or another facilitatory process, the key point is that the habituated response is reliably reinstated contingent upon the dishabituating stimulus. We believe this meets the established criteria for dishabituation.

(3.4) As behavioral facilitation of a habituated response can be achieved by dishabituating (specific recovery of the S-R pathway) and/or superimposed sensitizing (organism-wide) processes, dishabituation and sensitization of this olfactory response must be first dissociated; however, the study provided no evidence for the dissociation. Without this piece of evidence, the claim of this paper that the newly identified pathways mediate dishabituation is not fully supported.

We agree with the reviewer that we have not provided specific evidence dissociating dishabituation and sensitization of the particular olfactory response beyond the evidence implicating particular circuitry in the outcome of facilitation of the olfactory response.

It should be noted that in photoactivation of the implicated circuitries in naïve flies, we do not observe enhanced octanol avoidance, suggesting that activation of these circuits alone does not induce sensitization. Moreover, our results show that neither footshock nor yeast odor drive an organism-wide sensitization, as silencing specific circuits was sufficient to block dishabituation—something that would not be expected if a global sensitization process was responsible of reinstating the olfactory response.

Nonetheless, we will also attempt to dissociate sensitization from dishabituation using mutants previously reported deficient in sensitization (Duerr and Quinn, PNAS 1982), assuming these mutants retain normal olfactory habituation.We will also try sensitization protocols in the case of within-modal dishabituation to further clarify the underlying mechanisms. In principle, this includes using diluted Octanol as the habituating stimulus and attempt dishabituation with concentrated octanol.

(3.5) The literature review of this manuscript has some discrepancies. In the introduction, the authors wrote "initial studies in Aplysia were consistent with the "dual-process theory" (Groves and Thompson 1979), where response recovery due to dishabituation appeared to result from sensitization superimposed on habituation, thus driving reversal of the attenuated response (Carew, Castellucci et al. 1971, Hochner, Klein et al. 1986, Marcus, Nolen et al. 1988, Ghirardi, Braha et al. 1992, Cohen, Kaplan et al. 1997, Antonov, Kandel et al. 1999, Hawkins, Cohen et al. 2006)." Hochner 1986 and Marcus 1988 in fact indicated otherwise. Hochner 1986 suggests that dishabituation and sensitization involve different molecular processes, while Marcus 1988 showed that dishabituation and sensitization have different behavioral characteristics. Therefore, the authors' statement is not supported by the cited literature.

We are grateful to the reviewer for pointing out these significant discrepancies, consequent of multiple rounds of edits followed by our own oversight. These important publications for this manuscript will be referenced properly in the revised manuscript.

Author response:

eLife Assessment

The authors study global neuropeptide changes in C. elegans mutants lacking functional BMP, using this as a viable and fertile animal model that exhibits consistent dyspepsia and chronic dietary restriction. The findings of this study are valuable as they provide a global picture of neuropeptide responses to starvation and detail a circuit from a sensory neuron to lipid metabolism in the gut. This work provides evidence that nutrient stress resulting from impaired food processing engages NLP-10-, NPR-35-, FLP-18-, and NPR-4-dependent signalling to promote fat utilization. However, the evidence is incomplete, as the order of action of the neuropeptides is weak.

We thank Reviewing Editor, Senior Editor and the three reviewers for their constructive comments. We are encouraged that the reviewers regard the central finding that impaired pharyngeal function engages neuropeptide signaling to modify intestinal lipid metabolism as physiologically meaningful and supported by multiple lines of evidence. At the same time, we recognize that the reviews converge on a central concern: the evidence for the order of neuropeptides’ action is weak. The reviewers also suggest us to distinguish more clearly between what our experiments demonstrate and what we infer, to present the pathway as less strictly linear, and to be more explicit about the limits of cell-specific rescue for secreted peptides. We take these points seriously, and we are exploring possible revisions in light of them.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript describes how defective food grinding due to loss of TGF-beta signalling leads to fat loss via specific neuropeptides and their cognate receptors in C. elegans. They define transcriptional mechanisms from the ADL sensory neuron to neuropeptide relays from neurons to the gut, wherein enzymatic effectors mediate fat metabolism. The genetic evidence presented to support this neuropeptide circuitry is based largely on transcriptional changes detected in bulk mRNA, cell-type-specific rescue, and lipid measurements using Nile Red staining in permeabilized/fixed animals and with lipidomics. The findings are of interest to researchers in neuropeptide regulation of physiology.

Strengths:

(1) The multifaceted analysis of dbl-1 and sma-6 provides good evidence that the primary defect leading to metabolic phenotypes is due to pharyngeal function.

(2) The transcriptional survey of neuropeptide expression under fasting and in TGF-beta pathway mutants will be a useful resource for many labs studying neuropeptides in food sensing.

(3) Outlining the process from dietary restriction to fat metabolism in the gut provides a big-picture view that establishes physiological relevance.

(4) Identifying new functions for specific neuropeptides and their receptors in fat metabolism.

We thank R1 for an accurate summary and for recognizing the value of this work. We also note R1’s characterization of our evidence as transcriptional and genetic. We agree with this description and will explicitly state the scope of our claims in future versions, clarifying that this work defines a functional hierarchy among genes and cells but does not provide biochemical, electrophysiological, or secretion-based evidence for direct molecular interactions.

Weaknesses:

Evidence that links NLP-10-NPR-35 signalling to FLP-18-NPR-4 is weak, and primarily rests on overlaps in npr-35 and flp-18 expression, as well as rescue of flp-18 under the npr-35 promoter. It remains possible that FLP-18 acts from those neurons, but is not activated by NPR-35 signalling, since the mechanisms downstream of NPR-35 are unclear in this context. Strengthening this link would require showing a change in FLP-18 activity; for example, showing npr-35-dependent changes in flp-18 transcription in npr-35-expressing neurons.

We agree that this is the weakest link in our model. At present, this rests mainly on two observations: the overlap between npr-35 and flp-18 expression reported in public databases, and the ability of npr-35p::FLP-18 (or ttx-3p::FLP-18) to restore fat levels. These observations cannot exclude the possibility that FLP-18 acts from these neurons, or even from additional neurons, without being activated by NPR-35 signaling, and that the FLP-18 induction reflects the nutritional state rather than receptor activity.

To test this directly, we will begin by measuring flp-18 transcript levels in two comparisons: (1) well-fed npr-35(lf) versus well-fed sma-6(lf); npr-35(lf), and (2) well-fed npr-35(lf) versus fasted npr-35(lf). In addition, transcriptional levels of nlp-10, flp-1, and flp-4 can be compared in these worms. If NPR-35 activity is required for flp-18 induction when nutrients are limiting, removing npr-35 should blunt or reduce this induction in the sma-6-mutated or nutrient-deprived backgrounds; If NPR-35 activity is not required, flp-18 induction should not be affected. A third possibility is that NPR-35 amplifies FLP-18 signaling, which would not conflict with the nutrient-sensing role of FLP-18 per se. Regardless of the outcome, we will rewrite this section to clarify the step from NLP-10 to FLP-18.

The expression patterns of the neuropeptides and receptors that guide the sites of cell-specific rescue experiments are from well-fed animals. However, it remains a possibility that starvation alters neuropeptides and their receptors are expressed, which would produce a different circuit.

This is a fair point, and we accept it as a limitation of the present study. The expression patterns that guided our rescue experiments were defined in well-fed animals, using published datasets (Beets et al., 2023; Ripoll-Sánchez et al., 2023; Ghaddar et al., 2023) and our own transcriptional reporters under well-fed conditions. We cannot exclude that nutrient status alters the expression of these peptides and receptors.

We plan to examine intestinal npr-4p::GFP in well-fed and starved animals in the near future. We could also attempt to image neuronal npr-35p::GFP, but this would be technically challenging given mosaic expression and issues with worm orientation. In the Discussion of future versions, we will state this caveat and will be careful to describe our rescue experiments as identifying the cells in which a gene is sufficient to support the phenotype under the conditions tested, rather than as confirming the circuit in the starved animals.

Different food levels produce different physiological and transcriptional responses. The manuscript largely assumes that starvation is equivalent to food reduction when they are physiologically distinct states.

We agree, and we regret that our wording implied equivalence. Our intention was not to treat all nutrient-limited states as identical but to ask whether a common pathway is engaged. The observation that the same components are required under each of these energy-deficient conditions supports the physiological relevance of the pathway. We will rewrite the relevant sentences to convey this intent and to avoid implying that different nutritional states are equivalent. We acknowledge the limitation that our design cannot determine the degree of energy deficit required to engage the neuropeptides, or whether the response is graded across milder and more severe restriction.

Reviewer #2 (Public review):

Summary:

This manuscript investigates how animals adapt their metabolism to conditions of reduced nutrient availability. Using C. elegans, the authors identify a neuropeptide signaling network that promotes intestinal lipid mobilization when nutrient acquisition is compromised. The study proposes that nutrient stress activates signaling involving NLP-10, NPR-35, FLP-18, and NPR-4, ultimately leading to increased utilization of stored triglycerides.

A major strength of the work is the combination of multiple experimental approaches, including genetic analyses, neuron-specific rescue experiments, starvation paradigms, and lipid measurements. Together, these experiments support the conclusion that the identified neuropeptide pathway contributes to the regulation of energy stores during nutrient stress. The observation that similar signaling components function in both the mutant and starvation contexts strengthens the physiological relevance of the findings.

Strengths:

The revised manuscript is substantially improved and presents a coherent model linking sensory and interneuronal signaling to peripheral metabolic responses. The data convincingly establish functional roles for the identified neuropeptide components in controlling fat storage and mobilization.

Readers should keep in mind that the exact relationships among pathway components are not completely resolved. While the genetic evidence supports placement of NLP-10, NPR-35, FLP-18, and NPR-4 within a common regulatory framework, the data are somewhat less definitive regarding the precise order of signaling events and whether all interactions are direct. The authors appropriately acknowledge some of this complexity, and a clearer distinction between experimentally demonstrated versus inferred connections would further strengthen the presentation.

Overall, this is a carefully executed and biologically interesting study that advances our understanding of neuroendocrine control of metabolism during nutrient limitation.

Weaknesses:

No weaknesses were noted by this reviewer in the revision. My main comment is that whilst I appreciate the authors’ efforts to refine the signaling model in response to earlier comments, the pathway architecture remains somewhat complex, particularly regarding the relationships among NLP-10, NPR-35, FLP-18, and NPR-4. I encourage the authors to make one final pass through the text and model figure to clearly distinguish interactions that are directly supported by experimental evidence from those that remain inferred based on genetic relationships. This would help readers accurately interpret the strength of evidence supporting each step of the proposed pathway.

We are grateful to R2 for the positive assessment and for the constructive suggestions. We understand that the remaining concerns related to clarity and presentation. We agree that the pathway architecture remains complex and that readers should be able to distinguish experimentally connections from inferred ones. We will revise the text and the model figure accordingly. For example, future versions could use solid connectors for data-supported steps and dashed connectors for inferred steps.

We agree with R2 that readers should keep in mind that the exact relationships among pathway components are not completely resolved, and we agree and appreciate R2’s comment that “…the data are somewhat less definitive regarding the precise order of signaling events and whether all interactions are direct”, which echoes the suggestions from R1. We will address these points as outlined in our response to R1.

Reviewer #3 (Public review):

Summary:

In this manuscript, Liu et al. used C. elegans animals lacking functional BMP as a model to dissect the neuropeptide signaling pathways that lead to BMP-associated fat loss. First, they established the BMP mutants as a model of dyspepsia that results in chronic dietary restriction. They then used this model to identify neuropeptide genes that are upregulated and required for BMP-associated fat loss. Next, they sought to identify the receptors for these neuropeptides and to place the genes in a genetic and cellular pathway. They also showed that the same neuropeptides and receptors contribute to fat loss in diet-restricted C. elegans. They conclude that they have identified a neuropeptide signaling cascade in which impaired pharyngeal function activates sensory neurons, which then signal through interneurons to enhance triglyceride hydrolysis in the intestine.

Strengths:

In this manuscript, Liu et al. characterized the pharyngeal muscles and the intestinal bacterial context of animals lacking functional BMP. They showed a correlation between BMP-associated fat loss and pharyngeal impairments that could lead to insufficient food grinding. This finding suggests that C. elegans lacking functional BMP could serve as a model for dyspepsia and chronic dietary restriction. Moreover, the authors analyzed previously published gene expression data to identify neuropeptides that are overexpressed in animals lacking BMP. They then used mutants for these neuropeptides and their receptors to determine which of these genes contribute to BMP-associated fat loss. Finally, they showed that the same neuropeptides and receptors also contribute to fat loss in diet-restricted C. elegans.

We thank Reviewer 3 for a detailed assessment on this manuscript.

Weaknesses:

(1) The authors use double mutants between BMP pathway mutants and neuropeptide or neuropeptide receptor mutants to argue that the reduced fat levels of BMP mutants are suppressed. However, with the exception of unc-31, the fat content of the corresponding single neuropeptide or neuropeptide receptor mutant is not shown. Without these, the double-mutant phenotype cannot be interpreted as suppression, since it could reflect an independent effect on fat storage. To show that the effects are related to BMP signaling, the authors should compare wild-type animals to neuropeptide mutants in a sma-6(+) background. Similarly, the fat content of ADL-ablated animals is not shown in an otherwise wild-type background.

We accept this criticism. We are going to add experiments on wild-type and related single-mutant strains in the near future. Specifically, we will report the fat content of nlp-10(tm6232), npr-35(ok3258), flp-18(tm2179), flp-1(sy1599), flp-4(sy1606), and npr-4(tm1782), and of ADL-ablated animals, in the sma-6-functioning background. We will also survey published datasets for independent measurements of fat content in these strains, if any exist.

(2) In several places, the authors use cell-specific expression of neuropeptides to conclude that a given neuropeptide acts in a particular cell type (e.g., Figure 4B, C; Figure 5C, D). However, because neuropeptides are secreted and can act at a distance, expression in a non-native cell type may rescue the phenotype. These experiments therefore show sufficiency but do not establish the endogenous site of action. Cell-specific knockout or knockdown, or expression from control promoters in unrelated cell types, would help address this.

We agree with the underlying point of this criticism. Expression of a secreted peptide from a heterologous promoter demonstrates that the peptide can act when produced in that cell; however, it does not establish where the peptide acts under physiological conditions. We are grateful to the reviewer for these suggestions and have carefully considered both approaches. While we fully appreciate their potential value, we believe it is more appropriate to regard them as complementary rather than decisive, and we would like to explain our reasoning in detail.

The first approach, cell-specific knockdown, may or may not affect peripheral lipid catabolism in this system, because (1) the number of peptides capable of influencing fat storage is large, as shown in Figure 2 – figure supplement 1D, E, and (2) the expression pattern of a receptor or peptide gene may be altered under nutrient-deprived conditions (as in comments of R1). The axis we describe could be buffered by ligand redundancy, as our data on FLP-1 and FLP-4 show. Under such redundancy, a negative result from knocking down a single peptide in a group of cells would not exclude a physiological role for that peptide in that cell. The second approach, expression from a control promoter in an unrelated cell, might also be complicated by the point that R1 raises: if nutrient status alters the expression of peptides and their receptors, it becomes difficult to specify a cell type that is reliably “unrelated” to lipid regulation in the relevant physiological state. Therefore, we will modify our manuscript to describe the rescue experiments consistently as demonstrating sufficiency and discuss this limitation frankly.

(3) The authors report that expressing npr-35 from two promoters with non-overlapping expression each fully restores the low-fat phenotype of sma-6; npr-35 mutants. This is surprising for a receptor and is difficult to interpret.

We thank the reviewer for raising this point, and we realize that our description was not sufficiently precise. The two promoters drive expression in different subsets of npr-35-expressing neurons; however, in both cases npr-35 is overexpressed, as is typical of C. elegans transgenic lines. A non-exclusive explanation also seems plausible to us: the two cell populations (nmr-1-positive & ttx-3-positive) may converge on a shared downstream output, which is the release of FLP-18 from these interneurons, so that restoring receptor function in either population restores the ultimate output. We will revise the text to present both possibilities and to describe the result in terms of sufficiency.

(4) The authors identify neuropeptide genes co-expressed with npr-35 and follow up on flp-18. The rationale for restricting the search to co-expressed neuropeptides may bias hypothesis generation. Similarly, the authors show that flp-1 and flp-4, in addition to flp-18, contribute to BMP-associated fat loss, but only flp-18 is examined further because of its overlapping co-expression with npr-35, again creating a bias in the investigation of the role of neuropeptide signaling in BMP-associated fat loss.

We accept that restricting our attention to peptides co-expressed with npr-35 introduced a bias, and we will state this openly. We would like to note two considerations that may help contextualize this bias. First, flp-18 showed the strongest transcriptional induction among the peptides we examined (Figure 2 - figure supplement 1D), and this was an important reason for prioritizing it. Second, our subsequent analysis was not confined to co-expressed peptides: flp-1 and flp-4 are also required for BMP-associated fat loss, while flp-1 shows little overlap with npr-35 and does not appear to be released from npr-35-expressing neurons (Figure 5 - figure supplement 1D). The co-expression therefore served as an entry point rather than as a filter. We will clearly describe this rationale in the text, present the broader set of candidate peptides identified in our screen, and note that additional peptides are likely to contribute to fat regulation. We hope that the dataset will support work in this direction, both in our laboratory and in other laboratories.

(5) It is difficult to interpret the experiment in Figure 5E, where the authors conclude that npr-4 is required in flp-18-overexpressing animals. Without a demonstrated fat-loss phenotype from overexpressing flp-18, a requirement for npr-4 in those animals cannot be meaningfully assessed.

We assume that the reviewer is referring to Figure 5G, and we apologize for the confusion in this panel. This confusion may have arisen from the way we arranged the columns. The experiment was designed to ask whether npr-4 is required for overdosed FLP-18 to function (with overexpression ensured by sma-6(lf)-induced upregulation and the ttx-3p::FLP-18 transgene). Therefore, a clearer way to organize these columns would be to swap the third and fourth columns, which we will do in the revised version.

We nonetheless agree with the reviewer’s underlying point. Because ttx-3p::FLP-18 alone does not reduce fat in the already fat-deficient sma-6(lf), the assay has limited dynamic range. So, a requirement for npr-4 cannot be established from this comparison alone. We will reorder the columns, correct the legend, and present the panel as consistent with npr-4 acting downstream of flp-18. We would also place greater emphasis on the comparisons in Figure 5B, in which sma-6(lf); npr-4(lf) retained more fat than sma-6(lf); flp-18(lf), an outcome expected if the receptor acts downstream of the ligand and if additional ligands converge on NPR-4.

Overall, the authors convincingly identify neuropeptides and receptors that are overexpressed and that contribute to fat loss. However, several points make it difficult to fully support the proposed model and the linear pathway from the pharynx to the intestine through ADL sensory neurons and interneurons. These include the absence of phenotypic analysis of the single mutants, the challenges of interpreting cell-specific rescue experiments when studying neuropeptide function, the fact that additional neuropeptides causing BMP-associated fat loss are identified but not studied further, and results that do not necessarily point to a linear pathway (e.g., the triple mutant sma-6; nlp-10; npr-35 has a stronger phenotype than the double mutants with sma-6, the fat loss caused by overexpression of nlp-10 in a sma-6 background is not suppressed by npr-35, and the flp-18 overexpression experiment is difficult to interpret). The reviewer therefore suggests that the linearity of this pathway, and the sites of action of the neuropeptides and receptors, should be presented more cautiously or supported by additional data.

We are grateful for this synthesis, which we take as the central conceptual comment of the review. We agree that our data do not support a strictly linear pathway, and we will revise both the text and the model figure accordingly.

The two observations the reviewer cites, that the triple mutant sma-6; nlp-10; npr-35 retains more fat than either double mutant, and that removing npr-35 does not offset the fat loss caused by NLP-10 overexpression, point in the same direction: NLP-10 likely acts through receptor(s) in addition to NPR-35. We consider this plausible on independent grounds. Because nlp-10 is induced when nutrients are limiting, an additional receptor might be engaged only when NLP-10 rises above its basal level, or only when the nlp-10 expression domain expands under dietary restriction. Either scenario would explain why such a receptor has not emerged from interaction screens carried out under standard feeding conditions.

In the revision, we will describe the axis as a genetic framework in which the NLP-10/NPR-35 and FLP-18/NPR-4 modules are related, with branch points at both the ligand and receptor levels, and we will mark the connections that remain inferential. We will also note that the conservation of NPR-35 across nematodes (Beets et al., 2023; Golinelli et al., 2024) may provide an entry point for identifying additional NLP-10 receptors, and we would welcome works in that direction.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The manuscript could provide more nuanced and accurate context in several areas:

(1) Work from the Ashrafi Lab (Greer et al., 2008, Cunningham et al., 2014) has described roles for daf-7 (another TGF-beta) in fat metabolism and should be cited to provide a more comprehensive introduction.

Thanks! We will cite the work from the Ashrafi laboratory on the DAF-7 branch of TGF-β signaling and on fat metabolism in the Introduction of the revised manuscript.

(2) The interpretation of the unc-31 phenotype is not as straightforward as the text indicates. unc-31 does not only affect DCVs, unc-31 mutants also have SV defects. Moreover, DCVs also release TGF-beta and monoamines. Thus, an unc-31 phenotypes does not necessarily implicate neuropeptides.

We thank the reviewer for this comment and apologize for the confusion. In fact, in addition to analyzing unc-31(lf); sma-2(lf), we analyzed the fat levels of egl-3(lf); sma-2(lf) and egl-21(lf); sma-2(lf), and the phenotypes caused by the loss of egl-3 or egl-21 were similar to those caused by unc-31(lf) in these BMP mutants. We omitted these data from the previous version for simplicity, and we acknowledge that we wrongly overlooked the non-DSV roles of UNC-31/CAPS. We will revise this section by adding additional data on egl-3 and egl-21.

(3) In lines 132-134, the logic of the argument is not clear, since it does not indicate how sma-3 rescue in the pharynx is linked to sma-6 in the ADL neurons.

We agree with the reviewer’s comment and will remove the wording related to sma-3 rescue from this sentence in the revised manuscript.

(4) Lines 271-273 indicate that BMP mutants are mildly long-lived. This point is only partially correct. Depending on the food level, daf-7 mutants can be long-lived, have no phenotype, or be short-lived.

Thank you. We will rewrite the section on lifespan so that it reflects the lifespan of daf-7 mutants and BMP mutants properly.

This manuscript could also be improved by clarifying or acknowledging several technical gaps/weaknesses:

(1) For Supplemental Figure 2d, it is not clear if there is any correction for multiple hypothesis testing when assaying multiple neuropeptides. This point should be clarified.

We acknowledge that we did not perform any multiple hypothesis testing on the data shown in this figure panel in the previous version. Due to technical limitations, we were unable to compare all qRT-PCR groups within a single 96-well plate. The qRT-PCR assays were performed separately for each gene, with double mutant and single mutant worms collected in the same-day manner. Accordingly, these qRT-PCR results are not suitable for comparisons between different genes, but they do allow valid comparisons between the double mutant and the corresponding single mutant within the same target gene. We will clarify this point in the revised manuscript.

(2) Strains used in this work have only been outcrossed twice, which leaves 25% of mutations. The parent strains with tm and ok alleles were isolated after mutagenesis and are expected to contain thousands of mutations. Two outcrosses imply that several hundred unlinked mutations remain, which weakens the genetic evidence.

Because most of the data were obtained from double mutants (e.g., sma-6(lf); nlp-10(lf), sma-6(lf); npr-35(lf)), we performed at least one additional round of outcrossing by introducing the single mutants into the BMP mutants. We therefore expect that the background mutation load in these double mutants is lower than 25%. As we plan to do more experiments on the single mutants, we will first increase the number of outcrosses before measuring fat levels.

(3) More details are needed on the methods related to fluorescence microscopy, especially since most of the manuscript's conclusions rest on quantitative fluorescence. It is important to describe the light source and whether there was any calibration to control for variable fluorescence due to the equipment.

Thank you. We will do so. All Nile Red imaging was performed on the same microscopic system, which is not a confocal microscope but an upright widefield microscope, which captures the full depth of field along the z-axis (rather than a single optical section). In the revised manuscript, we will expand the fluorescence microscopy methods to describe the illumination source, the acquisition settings, and the measures taken, etc.

Reviewer #2 (Recommendations for the authors):

Minor Comments

(1) The finding that NLP-10 overexpression alone does not produce a strong phenotype in wild-type animals is intriguing. A brief discussion of how this observation fits into the proposed model would be useful for readers.

We agree with the reviewer that NLP-10 overexpression alone does not produce a strong phenotype in wild-type animals, which is intriguing. We have not yet performed a detailed mechanistic analysis of this phenomenon. We speculate that animals likely possess metabolic homeostatic mechanisms that buffer against perturbations in NLP-10 levels. As R1 suggested, it is also possible that dietary restriction or starvation conditions may broaden the expression range of nlp-10 or its receptor(s). We will discuss this possibility and its relationship to our proposed model in greater depth in the revised manuscript.

(2) Some figure legends describing complex genetic comparisons could benefit from additional explanatory language highlighting the key conclusion from each experiment. This would improve accessibility of the paper.

Figure legends will be improved in the revised version.

Overall Recommendation:

The manuscript has been substantially strengthened through revision, and the remaining issues are largely matters of clarity and presentation. I am supportive of the paper following minor revision.

Thank you again for your feedback. Revisions will include updated data and improved wording in future versions.

Reviewer #3 (Recommendations for the authors):

(1) dbl-1 mutants are mentioned in the Introduction without explanation. The authors should briefly describe what dbl-1 encodes and how it relates to the BMP pathway studied here.

We apologize for this confusion and will introduce DBL-1 properly in the Introduction by identifying it as the C. elegans BMP ligand that signals through the SMA-6/SMA-2/SMA-3/SMA-4 pathway.

(2) Lines 19, 60, and 238: It is unclear what exactly the authors mean by "mutant-specific effects," "mutant-specific phenomenon," and "mutant-specific mechanism."

We will replace the term “mutant-specific” with alternative wording. By this term, we meant “specific to BMP mutants”, as opposed to a general response to nutrient insufficiency.

(3) Lines: 56-57 The authors state that "the ADL sensory neurons release neuropeptide NLP-10... to promote the secretion of... FLP18". To make this statement, the authors need to use a neuropeptide secretion assay (e.g., the coelomocyte release assay) to show their claim or tone down the language.

We will tone down the language since we do not measure peptide secretion directly.

(4) ADL ablation in the sma-6; nlp-10 double mutant could help support the authors' hypothesis.

We agree that ADL ablation in sma-6(lf); nlp-10(lf) could in principle provide additional information. However, we do not consider this experiment essential for the revised manuscript. Our main concern is that metabolic regulation is mediated by many peptides with partially redundant and compensatory functions. Therefore, the outcome of ADL ablation in sma-6(lf); nlp-10(lf) would be difficult to interpret unambiguously. We will acknowledge this limitation in the Discussion of the revised manuscript.

(5) Figure 3D: The authors perform an ADL-specific rescue experiment to show that expression of sma-6 in ADL does not rescue the fat content defect of sma-6 mutants. Because this is a negative result, it is hard to interpret unless the authors first show that the construct is indeed expressed in ADL (e.g., by co-expressing a fluorescent reporter from the same transcript, such as in an operon with sma-6) and, second, that they can rescue the sma-6 phenotype by expression in the pharynx, especially if they want to support the model shown in Figure 3E.

We will either image ADL neurons expressing srh-220p::sma-6::sl2::gfp, using DiI filling as an ADL landmark, or test whether pharyngeal expression of SMA-6 rescues the phenotype.

(6) Figure 5G: the figure legend describes a different experiment than the one shown in the figure.

We will correct the legend for Figure 5G.

Minor points:

(1) Line 106: change "verify" to "verified".

(2) Line 134: change "might have worked" to "might work".

(3) Line 148: replace the ";" at the end of the phrase with a full stop.

(4) Figure 5- figure supplement 1E: the title reads "npr-4 is required in flp-10 overexpressed animals". The authors presumably mean "nlp-10-overexpressing animals".

We thank the reviewer for pointing out these flaws and will make corrections in subsequent versions.

Author response:

Thanks to the reviewers, reviewing editor and senior editor for their assessment of our manuscript. We summarize and address reviewer comments and suggestions below:

(1) The granularity of action selection is ambiguous (Reviewers 1 & 3)

(2) Consider neurons not modulated by movement (Reviewer 1)

(3) How to interpret ramp-like vs. abrupt changes in pre-movement firing rates (Reviewer 1)

(4) Population encoding could be considered a form of action selection (Reviewer 3)

(5) Improve the sample-size and screening of optotagging results (Reviewers 2 & 3)

(1) The granularity of action selection is ambiguous (Reviewers 1 & 3)

The reviewers astutely pointed out a critical ambiguity of the original action selection model: on what level are actions differentiated in the basal ganglia? Is it activation of specific muscles, or concerted movements of multiple body parts, or even complex sequences of behavior? Anatomically, the organization of striatonigral input as well as nigrocollicular pathways appear to be highly somatotopic (Foster et al., 2021; Lee et al., 2020), in the sense that there are parallel circuits that separately project to orofacial or skeletomotor regions of the superior colliculus (Benavidez et al., 2021). This might suggest an upper bound for the granularity of action selection in SNr, manifest at the level of tongue/jaw vs. limbs, different directions of reaching, or reaching vs. retraction. We tested these permutations and found little evidence for sign reversals in SNr responses. Nonetheless, one could always parse “action” into even finer components, or combine them into more complex ensembles or sequences of movements. It was exactly this logic that led us to test more and more movements, starting with different directions of reaching and culminating in the unbiased examination of spontaneous movement (Fig. 5, 6, 7). Nonetheless, we of course could not exhaustively exclude all movement possibilities/permutations, and our arguments are limited to the sets of actions that we tested. But we also point out that the granularity argument could be extended ad infinitum, to the point of being practically unfalsifiable! In the end, we will lay this logic out more clearly in the revised Discussion. (On the other hand, it is exactly this “granularity” conundrum that led us away from trying yet another movement paradigm, and toward the idea of examining functional connectivity between the SNr and SC, as outlined below.)

(2) Consider neurons not modulated by movement (Reviewer 1)

Reviewer 1 pointed out that unmodulated SNr neurons could be grouped with increase neurons, since they could maintain or increase inhibitory output in order to inhibit unwanted movements. Upon further inspection, we found 56/427 (13%) SNr units decreased firing for reaching but not for licking; conversely, 12/427 (3%) units decrease firing for licking but not for reaching; while 334/427 (78%) units increased firing or were unmodulated for both reaching and licking. In our original analysis excluding unmodulated SNr units, the proportions of units with congruent (86%) vs. incongruent (14%) signs of modulation for reaching and licking did not differ drastically when we included unmodulated units (78% vs. 16%). Nonetheless, this is a valid point, and we will include this in the revised Results and Discussion.

(3) How to interpret ramp-like vs. abrupt changes in pre-movement firing rates (Reviewer 1)

Reviewer 1 questioned how the slow ramp-like modulation of SNr firing relates to the disinhibitory gating model. We adopted the self-timed/spontaneous movement task not only to separate sensory vs. motor activity, but also due to clinical observations in Parkinson’s disease that patients are more debilitated for self-initiated rather than cued movements. We observed early pre-movement neural modulation in SNr during self-initiated movements, whereas Mink and Thach (1991) argued that pallidal activation was too late for movement initiation – albeit only in the context of cued movements. Slow ramp-like changes SNr firing does not contradict action selection per se, since modulation of SNr firing might need to reach some threshold level for a desired movement to occur, even in the context of action selection. On the other hand, these ramp-like changes might also represent a generic movement initiation signal without specifying which action to take. We pointed out the existence of ramp-like modulation during self-initiated movements, but the ramp-like nature of SNr modulation is not fundamentally incompatible with the gating model. We will clarify this point in the revised Discussion.

(4) Population encoding could be considered a form of action selection (Reviewer 3)

The reviewers also pointed out that while action selection is largely absent in single SNr neurons, licking vs. reaching could be efficiently decoded from population activity. Reviewer 3 reasonably asked: could population encoding be a form of action selection?

The answer, of course, is yes – but by the same token, any motor area that displays selectivity (motor cortex, thalamus, cerebellum, brainstem, etc.) could be argued to play a role in action selection. So what’s special about the basal ganglia? In this regard, it’s important to re-examine the basis for the action-selection hypothesis. The original model was put forward by Mink & Thach in 1991 to explain the paradoxical observation that most inhibitory pallidal output neurons increase rather than decrease firing during movement. The authors speculated that this increase population could inhibit unwanted movements, while the smaller decrease population could disinhibit the desired movement. The model has been tweaked here and there through the years, but the fundamental core of the idea has persisted, with little supporting evidence, presumably because it provides an explanation for the paradoxical increase neurons – an interesting explanation to be sure. However, if neurons that increase firing do so to inhibit an unwanted movement, then the simplest “other side of the coin” explanation is that they should decrease firing when that same movement is desired. Yet this sign-reversal motif was exceedingly rare among the SNr neurons in our study. Thus the critical question remains: why do so many pallidal output neurons increase firing with movement? We hope that one useful outcome of our study will be to stimulate others to think about pallidal responses outside of the action-selection framework.

Nonetheless, one could certainly argue that action selectivity is a prerequisite for action selection, and it may be worth asking how the SNr selectivity could contribute to this role. The SNr projects broadly to multiple brainstem and thalamic motor nuclei, which in turn affect specific movements. One could certainly devise wiring schemes whereby SNr outputs is parsed out among those downstream targets to mediate action selection. But these schemes are not exclusive to the SNr; they could pertain to any motor area with selectivity, nor do they provide an explanation for the paradoxical increase neurons. Nonetheless, R3’s thoughts likely reflect those of other readers, and we will try to lay out our logic more clearly in the revised Introduction and Discussion.

(5) Improve the sample-size and screening of optotagging results (Reviewers 2 & 3)

We used an optotagging technique to identify SNr neurons projecting to arm vs. orofacial SC and demonstrated that – during both reaching and licking – SNr neurons predominantly increased their inhibitory output regardless of their putative projection target. We think these results have important implications for the role of SNr output. However, the reviewers pointed out some critical limitations of our optotagging approach. Typically, to rule out polysynaptic confounds, light-evoked spikes are expected to have very low latency (typically a few milliseconds, but highly dependent on light power and opsin efficacy). However, it is unclear where the threshold for spiking latency should be drawn. Instead, to rule out polysynaptic confounds in our study, we relied on the fact we observed extremely few (<5%) silenced SNr neurons during optogenetic stimulation of a predominantly GABAergic region. Because SNr neurons send collateral GABAergic projections to other SNr neurons, optogenetic activation of a neighboring neuron should synaptically inhibit (rather than excite) a neuron of interest. Another possible source of contamination would have come from light leaking to into SC, which could have polysynaptically excited SNr neurons through the collicular-thalamic-striatal pathway. In this case, direct pathway striatal projection neurons should also suppress SNr firing. However, we did not observe any light-evoked inhibition among hundreds of putative SNr neurons, perhaps because viral labeling of neurons was sparse enough that polysynaptic inhibition was rare and largely unable to overcome optogenetic excitation. Therefore we did not suspect polysynaptic contamination among our results. Nonetheless, even after we had restricted our analysis to SNr units with low (<median) optogenetic responses latencies, the fraction of SNr units negatively modulated for reaching or licking was still extremely low (4% for reach among putative arm-SC projecting neurons; 8% for lick among putative orofacial-SC projecting neurons). We plan to collect additional data to address concerns regarding the smaller sample size.

References:

Benavidez, N. L., Bienkowski, M. S., Zhu, M., Garcia, L. H., Fayzullina, M., Gao, L., Bowman, I., Gou, L., Khanjani, N., Cotter, K. R., Korobkova, L., Becerra, M., Cao, C., Song, M. Y., Zhang, B., Yamashita, S., Tugangui, A. J., Zingg, B., Rose, K., . . . Dong, H.-W. (2021). Organization of the inputs and outputs of the mouse superior colliculus. Nature Communications, 12(1), 4004. https://doi.org/10.1038/s41467-021-24241-2 

Foster, N. N., Barry, J., Korobkova, L., Garcia, L., Gao, L., Becerra, M., Sherafat, Y., Peng, B., Li, X., Choi, J.H., Gou, L., Zingg, B., Azam, S., Lo, D., Khanjani, N., Zhang, B., Stanis, J., Bowman, I., Cotter, K., . . . Dong, H.-W. (2021). The mouse cortico–basal ganglia–thalamic network. Nature, 598(7879), 188194. https://doi.org/10.1038/s41586-021-03993-3 

Lee, J., Wang, W., & Sabatini, B. L. (2020). Anatomically segregated basal ganglia pathways allow parallel behavioral modulation. Nature Neuroscience, 23(11), 1388-1398. https://doi.org/10.1038/s41593-020-00712-5

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study describes targeting Poltheta Helicase with a new drug RP-3467. The properties of the drug and a clinical response in a gBRCA1 Ovarian Cancer Patient with a mutation in TP53BP1 are described.

Strengths:

This is an important and interesting set of observations.

We thank the reviewer for their positive assessment and appreciate their recognition of the significance and novelty of our findings.

Weaknesses:

(1) The response of the patient with a TP53BP1 mutant tumor is of interest but requires more clarification before solid conclusions can be drawn. The presence of the TP53BP1 mutation after but not before olaparib treatment is suggestive of selection, but in the absence of demonstration of a biallelic loss, this is conjecture. It could be a co-selected passenger mutation. The authors should report the TP53BP1 variant allele fraction, LOH, and orthogonal validation should be performed by targeted deep sequencing or ddPCR. This would establish the prevalence before and after selection and enhance the interpretation of the functional effects of the mutation observed.

We thank the reviewer for this important comment. We agree that identifying a TP53BP1 mutation after olaparib treatment does not, by itself, establish whether the mutation was directly selected under therapeutic pressure or represents a co-selected event, and we do not intend to make that distinction. Instead, we report that whole-genome sequencing (WGS) identified the TP53BP1 mutation in the tumor collected at the second debulking surgery. Importantly, an additional biopsy obtained at disease progression during the POLAR trial revealed a TP53BP1 variant allele frequency of 77%, with FACETS analysis identifying copy-neutral loss of heterozygosity (CN-LOH). These findings (new data in the paper) provide additional evidence consistent with biallelic inactivation of TP53BP1 and support the biological relevance of this alteration. Nevertheless, we acknowledge that these observations do not establish whether TP53BP1 loss directly drove acquired olaparib resistance, and we clarified this distinction in the revised manuscript.

(2) To further strengthen the proposed mechanism, the authors should consider knocking in the mutation (or a similar LOF mutation) into an appropriate cell line and establish resistance to olaparib and sensitivity to the combination, as well as each drug individually. This will address the latter question of whether it is the poltheta inhibitor or the combo that is responsible for the clinical response.

We thank the reviewer for this thoughtful suggestion and agree that establishing the contribution of TP53BP1 loss to treatment sensitivity is important for interpreting the clinical response. We would like to highlight, however, that this genetic relationship has been investigated in several published studies. Genetic depletion of POLQ has been shown to be synthetic lethal with 53BP1 or Ku70 deficiency (Wyatt et al., Molecular Cell, 2016; Feng et al., Nature Communications, 2019). More directly, Zatreanu et al. (Nature Communications, 2021) demonstrated that loss of 53BP1 or Shieldin components (SHLD1/SHLD3) in BRCA1-deficient cells confers resistance to olaparib while retaining sensitivity to the POLθ inhibitor ART558 as a single agent. These findings are further supported by Krais et al. and Ronson et al. (Nature Communications, 2023), who demonstrated POLθ dependency in BRCA1/53BP1-deficient backgrounds. Collectively, these studies provide strong genetic and pharmacological support for our proposed mechanism and suggest that POLθ inhibition itself may have contributed substantially to the observed clinical response. While we acknowledge that the relative contributions of RP-3467 and olaparib cannot be definitively distinguished in this patient, we believe that the existing literature provides a strong mechanistic foundation for interpreting this clinical observation, without necessitating additional genetic modeling in the context of the present study.

(3) In the animal experiments, "synergy" is overstating the situation. Without an interaction analysis, this is an enhanced combination activity. Also, several of the animal experiments have a small N. It would be better to show the growth of tumors in individual mice.

Although we believe that minimally in BRCA2-deficient CDX models (e.g. Fig. 2a,b) the term synergy is appropriate (no/minimal single-agent activity of RP-3467 and tumor regressions in combination), we replaced the term ‘synergy’ with ‘enhanced combination activity’ due to lack of a formal interaction analysis. Data from individual animals are included as Source Data.

(4) The authors propose that Poltheta inhibition could prevent the emergence of reversion mutations. This is not addressed in the paper, and if they want to suggest this, they should provide some evidence

We thank the reviewer and agree that the manuscript presents no data bearing on reversion mutations. The discussion should not have implied otherwise. We have rewritten relevant paragraph so that the idea is presented explicitly as an untested hypothesis arising from the microhomology signatures reported at reversion breakpoints by others.

Reviewer #2 (Public review):

Summary:

The authors set out to assess the in vitro potency of a new POLQ helicase inhibitor, assess its in vitro BRCA1/2 synthetic lethal properties, and confirm how it performs in vivo in PDX and cell line xenografts. The authors also show an anecdotal patient response with a PARP inhibitor + POLQ inhibitor combination.

Strengths:

This is a novel POLQi of the helicase activity. The anecdotal clinical response in a heavily pre-treated patient is interesting.

We thank the reviewer for their positive assessment and are pleased that they recognize the novelty of targeting the POLθ helicase activity and the potential clinical significance of the response observed in a heavily pretreated patient.

Weaknesses:

Most of these issues could be addressed by changes to the main text, i.e. by the authors describing limitations/caveats to interpretation, etc.

(1) The clinical anecdote is interesting but underanalyzed. It's difficult, though, to know one way or the other whether the PARPi+ POLQi treatment effect (only partial response) has anything to do with the 53bp1 mutation. There is a causative sign that the 53bp1 mutation could be the cause of PARPi resistance (the increase in 53bp1 mutation allele frequency in PARPi-naïve vs PARPi-resistant tumors), but no similar sign to show that the 53bp1 mutant tumor clone is targeted by POLQi treatment. For example, does 53bp1 mutation allele frequency fall in ascites or ctDNA during the course of treatment, or is the 53bp1 mutation lost in a tumor taken at the end of treatment?  

We thank the reviewer for this suggestion. While longitudinal monitoring of the TP53BP1-mutant clone would be informative, such data are unavailable. A biopsy obtained at progression on the POLAR trial revealed a TP53BP1 variant allele frequency of 77%, with copy-neutral LOH by FACETS analysis. Importantly, extensive preclinical evidence establishes synthetic lethality between 53BP1 deficiency and POLQ inhibition (Wyatt et al., 2016; Feng et al., 2019; Zatreanu et al., 2021; Krais et al., 2023), supporting a contribution of POLθ inhibition to the clinical response. Nevertheless, determining whether the response was driven by POLθ inhibition alone or its combination with olaparib will require evaluation in a larger clinical cohort.

(2) Although the relevant work is cited, the authors should be more explicit in the introduction and state that there is already evidence from 2 papers that Combined loss of BRCA1 and 53bp1 causes enhanced sensitivity to small-molecule POLQ helicase or polymerase inhibitors.

Agreed, and adopted. We changed the introduction to state this prior evidence explicitly on first mention, naming both studies and specifying that the effect has been demonstrated for inhibitors of Polymerase theta.

(3) Figure 4. Not exacerbating existing PARPi myelosuppression is great, but the authors have to acknowledge that the myelosuppression is still present when POLQ+ PARPI is used. Single-agent POLQi doesn't give myelotoxicity, but it also does not give strong anti-tumor efficacy. i.e. it would be fair for the authors to acknowledge this.

We agree with the reviewer and have revised the text to more accurately reflect these findings. While POLθ inhibition does not exacerbate PARPi-associated myelosuppression, it does not eliminate the hematologic toxicity of PARPi treatment. We also acknowledge that POLθ inhibitor monotherapy has limited antitumor efficacy in the models tested, highlighting the importance of combination treatment and the need to balance efficacy with tolerability.

(4) The increase in reticulocytes when mice are treated with POLQi could be a sign that there is an effect on myeloid lineages, but the animals are responding by increased production of this young myeloid lineage. Alternatively, this reticulocyte increase could drive or be a sign of pathology (polycythaemia vera, etc.). It would be good to see a commentary on this in the Discussion.

We agree, and updated the language in Results, page 9, to reflect this possibility.

(5) Re Figure 4. A therapeutic advance would be to see that, compared to other PARPi combinations such as platinum + PARPi or temozolomide + PARPi, a POLQ + PARPi combination doesn't give the same myelosuppression that these combinations do (by analogy, combined platinum + PARPi gives curative responses in mice but also wipes out the adaptive immune system). The authors need to add data showing the platinum+ PARPi positive control, or at the very least add a limitations of the study section to the manuscript to explain this fairly.

We thank the reviewer for this suggestion. The substantial myelosuppression associated with combining PARP inhibitors with platinum-based chemotherapy or temozolomide has been well documented in preclinical and clinical studies, including the references cited by the reviewer (Rajan et al., 2012; PMID: 24827126). We agree that a direct comparison would be informative. However, given that these toxicities are already established in the literature, we believe that repeating these experiments is not essential to the present study. We have instead clarified that our findings demonstrate that RP-3467 does not exacerbate olaparib-associated myelosuppression under the conditions tested, without implying that the combination is free of hematologic toxicity or has been directly demonstrated to be safer than other PARPi combinations.

(6) Figure 2 might give the impression that the new POLQi gives a similar, if not greater, BRCA2 synthetic lethal effect than a PARPi (e.g. 2d-f). It would help readers to see the full saruparib and olaparib dose-response curves, not (as per 2 A, B, C) just the single point estimates.

The ZIP synergy matrices in Extended Data Figure 2 were acquired across a full concentration grid for both agents, and therefore already contain the complete single-agent dose–response for olaparib and for saruparib in each line.

(7) Why was DOTC42510 not profiled for PARPi?

We apologize for the poor signposting that made this data hard to find. DOTC24510 cells were profiled with olaparib: the combination growth data appear in Extended Data Figure 2c and the corresponding ZIP synergy plot in Extended Data Figure 2d. The main-text sentence reporting the olaparib combination does name DOTC24510 alongside the two colorectal lines, but cites only the main-figure panels, which do not include this line.

(8) Figure 2f shows error bars on an n=2 dataset - one cannot estimate variance from only an n=2 dataset range.

We thank the reviewer for pointing this out. We agree that an n=2 dataset is insufficient for a reliable estimate of variability. We revised Figure 2f to show the data points without error bars and clarify the sample size in the figure legend.

(9) Is there a statistical analysis on Figure 2G?

The data originate from two independent experiments, so we did not consider it appropriate to perform a formal statistical analysis. We note, though, that the data were consistent between the two replicates and that a robust difference was observed between the combination and single-agent arms.

(10) Figure 3. Olaparib 25 mg/kg QD is well below the MTD in mice. This makes the olaparib response in HCT116 BRCA2 k/o xenografts look modest when compared to the combinations.

We used 25 mg/kg to highlight the strong combination potential between RP-3467 and olaparib. That said, Fig. 3b shows that even when a PARP inhibitor (saruparib in this case) is used at its maximally efficacious dose (PMID: 35929986), the RP-3467 combination has the potential to outperform PARPi monotherapy.

Reviewer #3 (Public review):

Summary:

The authors seek to validate the effectiveness of an inhibitor of the Pol theta helicase-like domain ATPase activity in its ability to ablate MMEJ activity in cell line models. They then confirm the inhibitor is synthetic lethal in a variety of BRCA1/2 deficient cancer models (and one PALB2 model). Finally, they report apparent effectiveness in treatment of a single patient that failed therapy with PARPi due to 53BP1 deficiency, a hypothesized special use-case for targeting pol theta.

Strengths:

It is a clear bench-to-bedside translation of mechanistic-oriented basic science to a clinical therapy. The experiments are largely rigorously performed. The approaches employed are impressively diverse, from in vitro to cell-line model, to preclinical model, to clinical application. The interpretations made are well supported by the available data.

We sincerely thank the reviewer for their thoughtful and encouraging assessment of our work. We are particularly pleased that the reviewer recognizes the translational significance of the study, the breadth and rigor of the experimental approaches, and the strength of the conclusions. We appreciate these positive comments and the constructive suggestions, which have helped us further strengthen the manuscript.

Weaknesses:

The addition of a few missing details would improve the usefulness to the reader. Additionally, the rationale behind some approaches could be clarified.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors identified transcription factor combinations capable of inducing retinal neuronal programs in cultured fetal human retinal pigment epithelial (RPE) cells. Using a pooled screening strategy, single-cell RNA sequencing, lineage barcoding, and immunohistochemical analyses, they identified ASCL1 and NEUROD1 as an effective combination for inducing retinal neuron-associated transcriptional states. This work aims to advance the development of therapeutic approaches for retinal regeneration by exploring the plasticity of RPE cells.

Strengths:

A major strength of the study is the comprehensive experimental design. The combination of transcription factor screening, lineage tracing, single-cell transcriptomics, and molecular validation provides a detailed characterization of the cellular responses to reprogramming factor expression.

Weaknesses:

All experiments were performed using fetal human RPE cells. Because fetal RPE remains relatively immature and retains proliferative capacity, it remains unclear to what extent the observed responses reflect true reprogramming of differentiated RPE cells versus activation of developmental plasticity already present in fetal tissue. The absence of adult human RPE controls limits assessment of the generality and translational relevance of the findings.

We agree with the assessment that the reprogramming of fetal RPE due to its potential fate plasticity poses a different challenge than the adult. In fact, embryonic chick RPE will only undergo neural trans differentiation when treated with FGF before embryonic day 4. Therefore, we specifically focused on RPE at early developmental stages for our experiments. It is interesting in that light that the ages of fetal human retina are far more advanced in their development than the E4 chick, yet still have the capacity for neural reprogramming; while it will be interesting to explore in the future how long during fetal development this plasticity exists, we were limited by the fetal ages that were available to us. Moreover, the facility that supplied our tissues (Birth Defects Research Lab) are no longer able to use NIH funds to distribute fetal tissues as they have for the last >40 years, making any future studies with primary fetal tissues much more difficult.

Reviewer #2 (Public review):

Summary:

This is an interesting study that explores how human RPE could be used as a source for new retinal neurons. This is a welcome addition to the field of retinal regeneration, which is currently focused almost exclusively on the regenerative capacity of Müller glia cells. The line of inquiry is firmly rooted in findings from amphibian and embryonic chick model systems and advances a fetal human retina RPE-based screening system as a rich resource for insights into human RPE biology, including as a potential stem cell source.

The authors investigate the potential of fetal human RPE cells to be reprogrammed into retinal neurons using overexpression of pro-neural factors. While this is a critical knowledge gap in the field of retinal regeneration with significant promise for developing regenerative therapies, several methodological concerns impact the interpretation of results. Firstly, while the authors sought to evaluate factors that enhance RPE reprogramming when co-expressed with ASCL1, nearly all co-expression constructs tested failed to achieve appreciable expression of ASCL1, leaving a central hypothesis of this study largely untested (Major concern 1). Second, although the authors were able to detect a cluster of photoreceptor-like cells in their screen, they were unable to identify which reprogramming construct generated this cluster (Major concern 2). Finally, an essential control that definitively demonstrates the value of combinatorial transcription factor reprogramming is missing (Major concern 3).

In summary, the authors establish a valuable new paradigm for culturing and reprogramming fetal human RPE, and even more importantly, demonstrate successful reprogramming to neural fates. However, the discussion and interpretation of results needs to be modified significantly to make it clear that (i) the outcome of many co-expression paradigms remains effectively unknown/untested due to failed over-expression of ASCL1, and that (ii) the reprogramming construct giving rise to photoreceptor-like cells could not be conclusively identified from their initial screen.

Strengths:

(1) Powerful new screening system advanced for exploring the regenerative potential of human fetal RPE cells.

(2) Co-expression vector system for testing additive effects of proneural transcription factors.

Weaknesses:

Major concerns:

(1) The authors executed a screen for combinations of factors that can enhance ASCL1-mediated reprogramming of RPE into retinal neurons. However, the expression level of ASCL1 was remarkably low in virtually all co-expression paradigms (see Figure 3C). Notably, the reprogramming combination with the highest potency (ASCL1 + NEUROD1) was also the one exhibiting the highest level of ASCL1 expression. The "failed" reprogramming of most of the co-expression constructs (ASCL1+LMO1, ASCL1+EZH2, and ASCL1+RAX2) is potentially a false negative resulting from low transgenic expression of ASCL1.

We agree with the reviewer that insufficient ASCL1 expression in the combinations might have led to lack of reprogramming, representing a false-negative result. We do not rule out that individual, rather than pooled, expression vectors of the “failed” varieties might prove effective. A future version of such a screen might need a control to test proper vector functionality of each member in the pool. However, the expression of ASCL1 alone from a vector in the same pool worked well. Additionally, the expression of ASCL1 from the ASCL1-NEUROD1 vector was not nearly as high as from ASCL1 alone and still led not only to reprogramming but also to a shift in the gene expression landscape as seen in 4D. This shift is consistent across experiments and vector constructs.

(2) The authors' interpretation is that the overexpression of NeuroD1 and Ascl1 generated a new cluster that expressed markers of photoreceptors such as RXRG and RCVRN (see Figure 3D). However, there does not actually appear to be any overlap between the ASCL1+NEUROD1 cluster (orange dots, left panel) and the cells expressing markers of photoreceptors (yellow/green/purple? /black? dots, right panel; yellow being ASCL1-EZH2, green being ASCL1, purple being ASCL1-and black being control - though color coding here is admittedly somewhat confusing). Thus, the photoreceptor-like cluster of interest actually seems to correspond to gray cells that were unmapped/exposed to an unknown programming cocktail. So, it remains completely unknown which reprogramming construct generated this cluster.

We apologize for the confusion in Figure 3D, which stemmed from lack of proper labeling.

The right panel shows the expression of photoreceptor genes in a feature plot, not the vector assignment. The color code is different between the left most panel (which shows vector assignment) and the other two panels (which show gene expression). To make this more clear, we have now separated this into a panel D and a panel D’, and added a caption as well as a scale bar for the D’ panel.

The reviewer is correct that the farthest subcluster with highest RCVRN/RXRG expression was not assigned ASCL1-NEUROD1 identity. The inherent sparsity of scRNAseq experiments and the small size of that particular cluster made definite identification challenging. Furthermore, vector assignment is tied to vector and thus barcode expression. It is conceivable that as cells matured towards a photoreceptor-like cells, they silenced the vector insertion locus but initiated marker expression. Additionally, these photoreceptor-like cells were assigned to the same cluster (neur, Fig. 3B) as the positively identified ASCL1-NEUROD1 cells by unsupervised clustering, express NEUROD1 (Suppl. Fig. 2D) and seem to follow the same trajectory. This suggests that they stem from ASCL1-NEUROD1 overexpression. Moreover, the follow-up experiments showing the expression of the relevant genes in the reprog4 cluster (Fig. 4) and the corresponding stainings (Fig. 5) provide evidence that ASCL1-NEUROD1 overexpression causes expression of RCVRN.

(3) To conclusively establish the additive role of NEUROD1 in reprogramming, it would be prudent to compare ASCL1 + FA directly to ASCL1+NeuroD1+FA. This control was not included but is needed for a more complete interpretation of results.

We thank the reviewer for this suggestion. Such a control would indeed clarify the role of FA treatment on reprogramming with ASCL1 alone. However, to address the additive role of NEUROD1, we presented in this study the comparison of ASCL1-NEUROD1 with ASCL1 alone. Even without the addition of FA, we noted a shift in expression pattern (Fig. 4D) and the formation of neurogenic clusters (Suppl.Fig. 4B) with the addition of NEUROD1. Moreover, as noted above, it is no longer possible for us to obtain tissue from the BDRL to carry out additional experiments at this time.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The antibody section should mention the dilution used and how primary antibodies were validated (in the current study, or cited from previous literature).

We have added the dilutions of the used primary antibodies. They are targeted against well-known markers in the field and have been validated by our lab and others.

(2) A supplementary table summarizing and comparing pro-photoreceptor genes detected vs functional photoreceptor genes would be helpful to readers.

We think that the heatmap in 4C provides a good overview of detected genes of interest.

(3) The manuscript would benefit if figures have scale bars and marker labels above or below the images, but not superimposed (so as not to block the gene signal in some cells). (Figure 1C).

We changed the labels in 1C and added a scale bar to be more consistent with the other figures in the manuscript.

(4) Figure 2B and 5B (neurogenic dome) are missing scale bars.

We added scale bars in 2B and 5B as well as the supplemental figures.

(5) Plasmid design: dual promoters without insulators should be addressed (MCV and Ef1a). If possible, an RPE65-specific promoter to drive ASCL1-NEUROD1, to show that short temporal expression is not capable of inducing the desired reprogramming.

We agree that an RPE-specific promoter would not only gauge the strength and duration that is necessary for reprogramming, but would also support translational efforts. While we have addressed that question somewhat with the HES1-ASCL1 construct in our initial experiments, more in-depth investigation to choose an optimal promoter will be necessary in the future.

Reviewer #2 (Recommendations for the authors):

(1) The first sentence of the abstract is identical to the third sentence of the introduction. Rephrase to avoid redundancy. There are currently a few promising approaches for treatment: for example, gene therapy to augment or replace mutated genes has proven successful in preclinical studies, and some of these therapies are moving towards the clinic [2], [3].

We rephrased the sentence to:

Current developments in gene therapy, which aims to deliver healthy copies of mutated genes, show promising results and are increasingly becoming available in the clinic.

(2) Panel 1C would be more informative if images were enlarged/zoomed in ~4x or higher.

We have enlarged the panels as requested by the reviewer.

(3) Panel 1D reports size/area differences for cultures at a variety of time points. Data should thus be represented as a line chart to reflect whether cell size is changing over time, rather than pooling data points from disparate time points into a single group.

We agree that such a chart would provide a measure of RPE maturation over time; however, our focus is the relationship between cultured and native RPE. As there seems to be little spread in the measurements between ages, and the range of ages between cultured and native RPE is comparable, we believe that the current chart represents a valid visualization.

(4) Panel 2D would be clearer if cluster labels were moved to the top of the figure (such that they sit above the columns corresponding to those clusters). It could be further clarified by adding category labels to the marker genes (i.e., RPE markers, ascl1 targets, Neural markers, etc.).

We thank the reviewer for this suggestion. We shifted the cluster labels and created new labels for the gene groups.

(5) No comma necessary here: Using transcription factor binding site analysis on these peaks, revealed an enrichment of members of the ETS family like ELK1/4 and ETV1/4.

Thank you for your attention to detail. We have removed that comma.

(6) Add dashed box to Panel 3D to indicate region of detail displayed in panels to the right (as was done in Panel 3C).

We have added a dashed box in panel 3D.

(7) Distracting typos in the legend of Figure 3.

We have corrected the typos.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors used FBDD screening to identify numerous compounds interacting with the ORF9b dimer. They expanded the original fragment hit, soaked the derivatives into the crystals and confirmed their binding poses, and showed that the derivatives bind the target with higher affinity. The authors further targeted the ORF9b binding site on TOM70, and used a fluorescence polarization-based (FP) assay to screen a compound library and obtained several hits. Structure-activity relationship (SAR) optimization yielded hit analogs that have higher binding affinity to TOM70.

Strengths:

(1) The study adopted novel drug design strategies, including stabilizing ORF9b homodimer to prevent it from binding TOM70, and blocking ORF9b from binding TOM70 by screening compounds that compete with ORF9b for binding TOM70.

(2) The work established a feasible high-throughput screening assay. This FP-based assay screened ~50,000 compounds, from which two hit compounds were further optimized to yield analogs with higher binding affinity.

We thank reviewer #1 for their thoughtful assessment of our work and their constructive feedback.

Weaknesses:

(1) The study lacks functional assays to evaluate whether the ORF9b-stabilized compounds or TOM70 binding compounds could affect IFN inhibition caused by ORF9b or virus infection.

We thank reviewer #1 for their feedback on this subject. We agree that cell-based assays measuring the impact of these compounds on IFN stimulation/suppression would be a valid next step. We have expanded the discussion section to include potential future experiments that could be conducted to probe this:

“Although we have not assessed the permeability of these compounds and their ability to restore IFN in the context of cell-based assays, one way this could be accomplished is by adapting a previously used reporter cell line. Specifically, this assay uses a reporter cell line that has a Lucia reporter under the control of the IFN-β/ISG56 promoter that is expressed upon mock infection with synthetic dsRNA. When WT Orf9b is co-transfected with the reporter, IFN is suppressed, and, we have shown that phosphomimetic mutants of Orf9b that block its interaction with Tom70 restores IFN signaling. If these compounds are sufficiently permeable, then, for the lipidated-compounds targeting the Orf9b homodimer, we would expect the Orf9b monomer: homodimer equilibrium to shift towards the homodimer due to the stabilizing effect these lipidated-compounds have on the homodimer conformation leading to an increase in IFN signaling. Similarly, for compounds targeting Tom70, we would expect that these compounds block the Orf9b monomer from binding to Tom70 to produce a similar effect.”

(2) There is a lack of experimental evidence to reveal the binding mode of lipidated-compounds with ORF9b homodimer.

- We thank reviewer #1 for their feedback. We agree that we were unable to provide direct evidence that our lipidated-compounds are bound to the homodimer through the central lipid-binding channel. Experimental structures of our compounds bound to the Orf9b homodimer would have strengthened our functional studies, however, as we described in the manuscript pertaining to our initial crystallographic fragment screen:

“Although we have shown that it is possible to refold the Orf9b homodimer to eliminate the lipid from the central channel, we found that apo-Orf9b homodimer crystals were far less tolerant to DMSO and on average diffracted to resolutions worse than 2.5Å. Importantly, we found that microseeding helped increase crystal reproducibility and yielded larger crystals on average. Therefore, for our crystallographic fragment screening campaign we elected to use the lipid-bound protein to identify additional potential binding sites that could be exploited to stabilize the Orf9b homodimer.”

- We did undertake efforts to co-crystallize our lipidated-compounds with refolded apo-Orf9b homodimers but were unable to generate crystals of sufficient quality to collect X-ray data. Therefore, we relied on both our fluorescence polarization assay and prediction models like Chai1 to investigate if the expected behavior could be recapitulated. We felt this was reasonable for three reasons.

- First, as we explain in the discussion, none of these compounds or structures were publicly available for models like Chai1 to train on which prevents data leakage:

“None of these structures were publicly available on the PDB prior to these structural predictions, therefore, they were not available for Chai1 to train on. The placement of the lipidated-analogs in the central channel was in line with the anticipated binding mode, albeit, with discrepancies between the predicted and structurally observed portions of the analog compounds.”

- Second, as we outlined in the fluorescence polarization assay, we tested these compounds in two control experiments that investigated whether the changes in FP signal over time could also be explained by the compounds binding to Tom70 directly, or, by acting on the obligate Orf9b monomer which was generated by truncating the N and C-termini:

“We first considered whether the lipidated-analogs had any binding activity for Tom70 on its own and whether changes in FP signal were due to binding to the Orf9b homodimer. We tested the compounds on their own in the presence of the pre-equilibrated Tom70:Orf9b-FITC complex and observed no significant decrease in FP signal indicating that the lipidated-analogs do not directly bind to Tom70 to drive a decrease in FP signal (Figure 2—figure supplement 2A). We next tested whether these compounds acted on the Orf9b homodimer specifically or if they could inhibit the Orf9b monomer from binding to Tom70 by incubating compounds with an Orf9b peptide that acts as an obligate monomer. When chasing with the pre-equilibrated Tom70:Orf9b-FITC complex, we observed no significant differences in kinetics of Orf9b peptide binding compared to the peptide on its own which showed a fast single-exponential kinetic decay in signal suggesting that these compounds do not act on the Orf9b monomer to inhibit binding to Tom70 (Figure 2—figure supplement 2B)”

(3) There is a lack of experimental evidence to reveal the binding mode of HTS hits or analogs for TOM70.

We thank reviewer #1 for their feedback. We agree that experimental structures of our HTS compounds bound to Tom70 would provide more insights into how these compounds bind to Tom70 (and their precise location) in ways that the predicted complexes from models like Chai1 were unable to do. At the time of drafting this manuscript, we had not yet identified suitable conditions for structurally resolving Tom70 with our HTS compounds. Therefore, we elected to rely on two orthogonal methods of predicting where our HTS compounds are bound to probe whether the predicted binding sites could plausibly block Orf9b from binding. In the time since releasing this manuscript, one group had been able to crystallize apo-Tom70 which may serve as a suitable platform for future structural studies investigating these compounds and their exact binding mode to Tom70 to enable structure-guided optimisations of these initial hits.

(4) Overall, none of the compounds shown in the paper have promising potency warranting further development; their binding affinity is limited to the micromolar range.

We thank reviewer #1 for their feedback. We agree that these compounds should be viewed as starting points for potential future optimization on targets where there were no previous existing ligands. The molecules serve to validate that it is possible to develop small molecules that target Tom70’s C-terminal domain which may be relevant to future studies investigating Tom70’s biology.

Reviewer #2 (Public review):

Summary:

The authors investigate chemical strategies to disrupt the interaction between the SARS-CoV-2 accessory protein Orf9b and the host mitochondrial receptor Tom70, an interaction implicated in suppression of type-I interferon responses. They employ two discovery approaches: a crystallographic fragment screen against the Orf9b homodimer and a high-throughput fluorescence polarization screen for compounds that compete with Orf9b binding to Tom70. The study identifies fragment-binding hotspots on Orf9b, develops lipidated analogs that stabilize the Orf9b homodimer, and discovers Tom70-binding compounds with low micromolar activity that inhibit Orf9b binding in vitro.

Strengths:

An impressive amount of work using a variety of complementary approaches and methods to validate binding (FP, SPR, and computational modelling and SAR). The combination of crystallographic fragment screening on Orfb9 and HTS on Tom70 provides two independent routes for perturbing the Orf9b-Tom70 interaction. The structural work seems to be of very high-quality. The fragment campaign is extensive, yielding a substantial number of fragment-bound structures and identifying biologically meaningful binding hotspots on Orf9b.

Finally, the screen results in reporting useful chemical starting points. Although potency remains modest, the study provides tractable scaffolds and a clear framework for future optimization.

We thank reviewer #2 for their thoughtful assessment of our work and their constructive feedback.

Weaknesses:

General comment:

(1) Although there is already an incredible amount of data presented, one limitation of this study is the lack of cellular validation - do these drugs enter cells, restore interferon signalling, reduce viral loads, or alter Orfb9 localization?

We thank reviewer #2 for their feedback. See also the feedback from Reviewer 1. We have not assessed the permeability of these compounds in the context of cell-based assays and IFN signaling and agree that cell-based assays measuring the impact of these compounds on IFN stimulation/suppression would be a valid next step. We have expanded the discussion section to include potential future experiments that could be conducted to probe this:

“Although we have not assessed the permeability of these compounds and their ability to restore IFN in the context of cell-based assays, one way this could be accomplished is by adapting a previously used reporter cell line. Specifically, this assay uses a reporter cell line that has a Lucia reporter under the control of the IFN-β/ISG56 promoter that is expressed upon mock infection with synthetic dsRNA. When WT Orf9b is co-transfected with the reporter, IFN is suppressed, and, we have shown that phosphomimetic mutants of Orf9b that block its interaction with Tom70 restores IFN signaling. If these compounds are sufficiently permeable, then, for the lipidated-compounds targeting the Orf9b homodimer, we would expect the Orf9b monomer: homodimer equilibrium to shift towards the homodimer due to the stabilizing effect these lipidated-compounds have on the homodimer conformation leading to an increase in IFN signaling. Similarly, for compounds targeting Tom70, we would expect that these compounds block the Orf9b monomer from binding to Tom70 to produce a similar effect.”

(2) The logic of locking Orfb9 as a dimer is that the monomer binds Tom70 - thus, a more stable dimer means less monomer. In Figure 2, the Orfb9 homerdimer stabilization by compounds should reduce binding affinity to Tom70. A direct binding experiment measuring reduced Tom70 binding with compound treatment would better strengthen this claim.

We thank reviewer #2 for their observation and agree that compounds targeting the Orf9b homodimer conformation should block binding to Tom70 by preventing Orf9b homodimer dissociation into Orf9b monomers. As schematized in Figure 2D, we described how our fluorescence polarization assay measures the binding of Orf9b to Tom70. It provides insight into how compounds that bind to the Orf9b homodimer may slow the rate of homodimer dissociation. In addition, we have previously demonstrated in a separate publication that there are clear differences in the Orf9b homodimer dissociation kinetics when using either lipid-bound or lipid-free Orf9b homodimers as the competitor due to the stabilizing effect the lipid has on the homodimer conformation.

Reviewer #3 (Public review):

Summary:

This paper attempts to and succeeds in demonstrating that Orf9b is able to bind small molecules using X-ray fragment screening, SPR and FP assays. Exploration of sites from the fragment screening is performed along with fragment linking with inter-dimer lipid moieties.

Strengths:

The experimental work looks strong and well performed. The interpretation of the data is appropriate and was often validated through orthogonal methods and follow-up compounds. The use of Tom70 to find binders that might disrupt interactions between Orf9b and Tom70 is elegant.

Weaknesses:

The use of Chai-1 to predict co-folded structures with binding molecules was not properly described - no mention of this in the methods. It was not commented on whether the compounds which were found were attempted to be co-crystallised. If they were but negative data was collected (didn't crystallise, didn't diffract or no additional density was found), then this needs to be stated.

We thank reviewer #3 for their feedback. We have revised the manuscript to clearly point out that beyond our initial attempts to crystallize apo-Orf9b homodimer to enable fragment soaking, we also attempted to both soak our lipidated-compounds into apo-Orf9b homodimer crystals as well as co-crystallize the compounds which did not yield crystals.

“We attempted two strategies of crystallizing our lipidated-compounds with the apo-Orf9b homodimer to structurally resolve the complex. First, we attempted to soak our compounds into apo-Orf9b homodimer crystals but observed poor tolerance to DMSO which quickly disintegrated the crystals after minutes. Second, we attempted to co-crystallise the lipidated-compounds after refolding the Orf9b homodimer to generate apo-Orf9b homodimers but could not identify conditions that yielded crystals upon re-screening.”

We have also revised the methods and materials section to better explain the use of Chai1 to co-fold both Orf9b and Tom70 with their respective compounds.

“Chai1’s web server was used for co-folding either Orf9b or Tom70 with their respective hits. For the Orf9b homodimer, the sequence for a single chain was supplied to represent chains A and B in the homodimer and the ligands were supplied as SMILES strings. In the case where two copies of the ligand were investigated, the number of copies of the ligand was increased to two. Co-folding was performed using MMSeqs2 for the MSA and template searching to ensure the correct folding of the homodimer conformation. Tom70 co-folding was performed by supplying the sequence for hTom70 as a single chain and the compounds as SMILES strings. Co-folding was performed using MMSeqs2 for the MSA with template searching.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) It is disappointing that the authors screened binders for ORF9b homodimer, identified hits and derivatives binding at sites 1 & 2, measured the binding affinity to the target, but found no effects on stabilizing ORF9b homodimer. The FP competition assay was used to assess the efficacy of the compounds; maybe the authors could use alternative methods like Thermal Shift Assay (TSA) assays to detect some subtle changes in stability.

We thank the reviewer for their comments and agree that the lack of stabilizing activity observed for the site 1 and 2 analogs was disappointing. However, we do feel that the lipid-binding central channel may be a viable alternative site target that may also yield insights into the role of lipid binding in Orf9b biology. We agree that orthogonal methods such as TSA could be insightful for probing the stabilizing effects of the compounds on the Orf9b homodimer.

(2) To better illustrate the results of the FP kinetic assay to investigate whether lipidated-compounds binding to the Orf9b homodimer had effects on the stability of the Orf9b homodimer and Orf9b-Tom70 equilibrium, I recommend moving the results shown in Supplemental Figure 4 to a main figure and merging these results with Figure 2CD.

We think that the eLife publication platform provides appropriate visibility for the supplementary figures and that Figure 2D does the best job of illustrating the effects on kinetics for the initial reader.

(3) Have the authors tried to co-crystallise their top-rated lipidated-compounds with ORF9b homodimer to see where the lipid part of the compound could extend into the central channel of ORF9b homodimer?

We have revised the manuscript to clearly point out that beyond our initial attempts to crystallize apo-Orf9b homodimer to enable fragment soaking, we also attempted to both soak our lipidated-compounds into apo-Orf9b homodimer crystals as well as co-crystallize the compounds which did not yield crystals.

“We attempted two strategies of crystallizing our lipidated-compounds with the apo-Orf9b homodimer to structurally resolve the complex. First, we attempted to soak our compounds into apo-Orf9b homodimer crystals but observed poor tolerance to DMSO which quickly disintegrated the crystals after minutes. Second, we attempted to cocrystallize the lipidated-compounds after refolding the Orf9b homodimer to generate apo-Orf9b homodimers but could not identify conditions that yielded crystals upon re-screening.”

(4) Have the authors tried to co-crystalize hit compounds or hit analogs resulting from SAR with the TOM70 protein, to really observe the binding mode of these compounds? Only using in silico methods is not satisfactory.

We initially attempted to develop a crystallization system for Tom70 that would enable us to structurally resolve our bound compounds, but, at the time of writing the manuscript, had not identified a system that yielded crystals. However, another group has published a structure of apo-human Tom70 (https://pmc.ncbi.nlm.nih.gov/articles/PMC13075491/) - we sent them compounds and were unable to identify convincing density by soaking. We agree that a future study in a different crystal system or by pursuing co-crystallization could be fruitful.

(5) Although the authors improved the binding affinity of HTS hits for TOM70 using SAR, there is a lack of functional assays to evaluate whether the HTS hits or analogs could affect IFN inhibition caused by ORF9b or virus infection (cell-based or animal-based assays).

We have expanded the discussion section to include potential future experiments that could be conducted to probe this:

“Although we have not assessed the permeability of these compounds and their ability to restore IFN in the context of cell-based assays, one way this could be accomplished is by adapting a previously used reporter cell line. Specifically, this assay uses a reporter cell line that has a Lucia reporter under the control of the IFN-β/ISG56 promoter that is expressed upon mock infection with synthetic dsRNA. When WT Orf9b is co-transfected with the reporter, IFN is suppressed, and, we have shown that phosphomimetic mutants of Orf9b that block its interaction with Tom70 restores IFN signaling. If these compounds are sufficiently permeable, then, for the lipidated-compounds targeting the Orf9b homodimer, we would expect the Orf9b monomer:homodimer equilibrium to shift towards the homodimer due to the stabilizing effect these lipidated-compounds have on the homodimer conformation leading to an increase in IFN signaling. Similarly, for compounds targeting Tom70, we would expect that these compounds block the Orf9b monomer from binding to Tom70 to produce a similar effect.”

(6) Figure 4 doesn't have A, B, or C indicated in the figures.

We have revised Figure 4 to include A, B, and C.

Reviewer #2 (Recommendations for the authors):

(1) Page 5 line 23: The authors could comment on the biological relevance of the lipid-bound version of Orfb9 and how it could associate with membranes.

We thank the reviewer for their comments. Currently, it is unknown what role lipid-binding plays on Orf9b’s function beyond the stabilizing effect it has on the homodimer conformation. While it has been shown that Orf9b co-localizes at the outer mitochondrial membrane through Tom70 association, it has not been shown that Orf9b itself binds to membranes. While this does not exclude the possibility that the Orf9b homodimer could directly bind to membranes, we suspect a more plausible explanation is that Orf9b homodimers can bind to lipid-like metabolites within cells such as palmitate which we had previously shown.

(2) Figure 3F: These SPR sensorgrams are not all to the same y-axis scale.

We thank the reviewer for their comment. The sensorgram axis scale is reflective of three separate SPR experiments on three capture points for the ligand. Therefore, differences in ligand capture on each surface will produce slight differences in the total measured response. The axes are scaled to make interpretation easier. We are not quantitatively comparing between treatments, but noting the qualitative behavior of each individually as the concentrations change.

(3) Discussion: The authors could comment on the next steps, ligands ADME, solubility, permeability as the compounds are at low uM binding affinity, with increased concentrations, comment on selectivity/specificity.

Given that these are still “hits”, we think a discussion of these properties (which we study intently in the lab!) is premature and beyond the scope of this manuscript.

Reviewer #3 (Recommendations for the authors):

(1) The authors should carefully read the manuscript as there are numerous typos and duplicated words across the whole document and supplementary data.

We have gone through the manuscript and the supplementary material and corrected the typographical errors and duplicated words that we found, including a repeated sentence in the crystallization methods and a repeated word in the purification methods. We have also renamed the supplementary figures to the eLife figure supplement style. We expect copy editing at the VOR stage to catch anything that remains.

(2) Details of how Chai-1 was run, including constraints, should be given in the Materials and Methods section.

We have revised the methods section to describe how Chai-1 was used for both Orf9b and Tom70 co-folding predictions. See above.

(3) There was no comment on whether the compounds which were found were attempted to be co-crystallised. If they were, but negative data were collected (didn't crystallise, didn't diffract, or no additional density found), then this needs to be stated.

We have revised the manuscript to clearly point out that beyond our initial attempts to crystallize apo-Orf9b homodimer to enable fragment soaking, we also attempted to both soak our lipidated-compounds into apo-Orf9b homodimer crystals as well as co-crystallize the compounds which did not yield crystals.

“We attempted two strategies of crystallizing our lipidated-compounds with the apo-Orf9b homodimer to structurally resolve the complex. First, we attempted to soak our compounds into apo-Orf9b homodimer crystals but observed poor tolerance to DMSO which quickly disintegrated the crystals after minutes. Second, we attempted to co-crystallize the lipidated-compounds after refolding the Orf9b homodimer to generate apo-Orf9b homodimers but could not identify conditions that yielded crystals upon re-screening.”

Author response:

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

We thank the editors and reviewers for their careful and constructive assessment of our manuscript. Based on their comments and suggestions, we have revised the manuscript extensively to improve accessibility, clarify model novelty and the physical intuition behind the wave directionality, and correct and expand figures, units, equations, parameter definitions, and references.

The main changes in the revised manuscript are that:

- The abstract and main text now explicitly describe the work as coupling established reaction–diffusion models of Cyclin B–Cdk1 signaling and the excitable Rho–actin cortex, rather than presenting the individual modules as newly developed models.

- The governing equations, model assumptions, coupling, and key parameters are presented in the main text, with clarified units and a complete parameter table.

- Figures 1 and 2 were redesigned to make the geometry, kymographs, wave-front/wave-back definitions, and coexistence of travelling-wave-like and diffusive dynamics more intuitive.

- The diffusion-coefficient units and the conversion used to calculate total active nuclear Cyclin B–Cdk1 were corrected; the affected plots were regenerated and total active nuclear content is now defined explicitly in Eq. 7.

- The Introduction and Discussion now better distinguish established Cdk1–cortex coupling from the contribution of this study, incorporate work in Drosophila and zebrafish, and distinguish experimentally supported observations from model predictions.

- The cortical dynamical regimes and the role of Ect2 were clarified, supplementary figures were revised, and the suggested classic references were added.

eLife Assessment

This valuable study combines previously established mathematical models to investigate why cortical waves in starfish and Xenopus embryos propagate in opposite directions. The modeling results are solid and plausible, but remain experimentally untested. Improving the presentation and discussion of the results could make the study more accessible to a wider audience.

We appreciate this assessment and have focused the revision on exactly these points. The manuscript now makes the established origin of both model modules explicit, provides the core equations and parameters in the main text, gives a more intuitive explanation of the front–back mechanism, redesigns the key figures, and expands the discussion of experimental support, limitations, and testable predictions. The work remains theoretical, and we now state that limitation more clearly rather than implying experimental validation. See Abstract, Introduction, Model, and Discussion in the revised manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The main goal of this manuscript is to develop a mathematical model of the regulation of cortical dynamics by Cdk1 activity to explain why, in some embryos (e.g., Xenopus), surface contraction waves are believed to move in the same direction as Cdk1, while in other embryos (e.g., starfish) they are believed to move in the opposite direction.

Strengths:

(1) The paper addresses a very important question.

(2) The mathematical model is sensible and suggests that the different relationship between Cdk1 and surface contraction waves might arise from the different behavior of the mitotic entry wave and the mitotic exit wave.

(3) The authors propose a mechanism by which the wave observed at mitotic exit might not passively follow the trigger wave observed at mitotic entry'

(4) The proposed mechanism is a potential explanation of the observed differences.

(5) The proposed mechanism is centered on different dynamics between the nucleus and the cytoplasm, highlighting the potential importance of the nucleus (and nuclear size) in organizing cortical dynamics.

We thank the reviewer for this positive assessment. The revision now makes the central question and the scope of the contribution more explicit: the individual Cdk1 and cortical modules were already previously established, while the present study asks how their coupling, together with cell geometry and nuclear Cdk1 content, can generate distinct wave-back dynamics and cortical responses. The revised manuscript now also foregrounds the mechanistic distinction between activation fronts and wave backs and uses this distinction to organize the Results and Discussion sections. See Abstract, Introduction, Results and Discussion in the revised manuscript.

Weaknesses:

(1) The proposed mechanism works if the activity in the nucleus is much higher than the high activity (high state of the bistable system) of the cytoplasm. So, as the wave propagates across the cytoplasm, the activity around the nucleus remains higher, which potentially causes a delay in the onset of Cyclin B-Cdk1 degradation in the region around the nucleus compared to the surrounding cytoplasm. This effect happens over a typical length scale, and if such a length scale is comparable to embryo size, this becomes the predominant mechanism. However, such a mechanism should exist near the nucleus independently of embryo size. So, it seems that for embryos where the wave back and wave front should travel together, nuclear activity must be adjusted not to be much higher than cytoplasmic activity. A better discussion of the discovered process and its implications would strengthen the paper. It requires careful reading to understand what, in hindsight, is a rather simple explanation. Is there any experimental evidence that the overall activity of Cdk1 is higher in the nucleus than in the cytoplasm?

We agree that the mechanism needed a more intuitive explanation. The revised Results now separate two simultaneous processes. The activation front propagates outward with an approximately constant trigger-wave-like velocity, whereas excess active Cyclin B–Cdk1 associated with the enriched nuclear pool also spreads diffusively. This diffusive component exists locally around the nucleus irrespective of cell size. What depends on effective system size is whether that diffusive length scale is large enough, relative to the cell, to shape the wave back over a substantial fraction of the domain and ultimately at the cortex. This is why nuclear content and effective system size act together. The revised Fig. 2B and the accompanying text now explain this competition explicitly. We also revised the Discussion to distinguish experimental plausibility from quantitative validation: active Cyclin B–Cdk1 has been observed to accumulate in nuclei before surrounding cytoplasmic activation in frog egg extracts, nuclei can specify where mitotic waves begin, and Cyclin B enrichment near the nuclear region has been reported in starfish oocytes. However, whether nuclear active Cyclin B–Cdk1 reaches the level required for complete wave-back reversal remains a model prediction, which we now state explicitly. See Results, Fig. 2B and caption (p. 6), Methods and Eq. 7 in the revised manuscript.

(2) While the fact that Cdk1 can enslave cortical dynamics is clearly shown in the model, this is expected from the literature. There are systems where the enslavement of cortical and bulk actomyosin contractility to Cdk1 activity has been more clearly demonstrated (Drosophila and zebrafish embryos), as well as shown to have clear functions (nuclear positioning and ooplasmic segregation).

We agree. The revised manuscript no longer presents Cdk1 control of cortical dynamics as a novel result. We expanded the introduction to discuss Drosophila and zebrafish and to note the established functions of Cdk1– actomyosin coupling in nuclear positioning and ooplasmic segregation. We now frame the contribution of the present work as explaining how established Cdk1-to-cortex coupling can transmit geometry-dependent cytoplasmic waveforms into different cortical directionality and reactivation regimes. See Introduction and Discussion in the revised manuscript.

(3) The writing could be improved. The authors make some claims of originality that seem a stretch, e.g., in the abstract, they say: "we develop a reaction-diffusion model of Cyclin B-Cdk1 signaling in spherical cells with localized nuclear activation", but they essentially use a previous model with a few numerical tweaks. The figures are sometimes mislabelled or not explained, and some of the units seem wrong.

We agree and revised the framing throughout. The Abstract now states that we “couple established reaction–diffusion models of Cyclin B–Cdk1 signaling and the excitable Rho–actin cortex.” The Introduction similarly states that we are not developing a new model, and a dedicated Model section now gives the equations, assumptions, coupling, and original sources of the two modules. We also revised figure labels and captions, added schematic panels, corrected the diffusion units to μm²/s, corrected the conversion used for total active nuclear Cyclin B–Cdk1, and regenerated the affected plots. The control variable is now defined explicitly as total active nuclear content in Eq. 7 and reported in pmol. See Abstract, Introduction, Model, Fig. 1 and caption (p. 3); Fig. 2 and caption (p. 6); Methods, especially Eq. 7 and Table 1 (p. 16) in the revised manuscript.

(4) The authors give the existence of trigger waves as a fact. While the predominant view is that such waves exist in the first cycle of the Xenopus embryos (however, this is from measurement of the cortical contractions, so a bit circular for this paper), it is unclear if waves exist in the starfish embryo, so the potential explanation that the starfish embryo simply has different Cdk1 dynamics cannot be ruled out.

We agree that the evidence is not equivalent across systems. The revised manuscript avoids treating a starfish intracellular Cdk1 trigger wave as an experimentally established fact and instead presents the cross-species comparison as an interpretation within the model framework. We distinguish the model prediction from the available experimental observations and explicitly state that the nuclear active Cyclin B–Cdk1 level required for complete waveback reversal remains to be tested. Thus, different underlying Cdk1 dynamics in starfish are not excluded by our study. See Introduction, Results and Discussion in the revised manuscript.

Reviewer #2 (Public review):

Summary:

Large oocytes show prominent waves of cortical contractions. Previous works combining experiments and computational modeling have shown that the waves are driven by gradients of CDK1 kinase activity that trigger excitable Rho activity patterns on the cortex. This present work combines two previously published mathematical models for CDK1 activation and Rho activation, respectively. They show that the models combined can explain diverse shapes of cortical contractions observed in different species and at various stages of development. This shows how the same molecular machinery can generate diverse patterns dependent on the size of the system and the size and position of the cell nucleus.

Strengths:

(1) Carefully done modeling work providing a simple and elegant explanation for a complex cellular behavior.

(2) Very nicely illustrated, simulations can be directly compared to previous experimental observations.

(3) Explains observations made in different model systems, providing a unifying model.

We thank the reviewer for this assessment. We have revised the manuscript so that this scope is explicit from the outset: the model modules are established, while the contribution is the analysis of their coupling and the identification of geometry, total nuclear Cdk1 content, and cortical recovery kinetics as controls that generate qualitatively different behavior within one framework. See Abstract, Introduction, Results and Discussion in the revised manuscript.

Weaknesses:

(1) Purely theoretical work, no experimental validation.

We agree that direct experimental validation would strengthen the work. We have not added a new experimental dataset in this revision. Instead, we have made the experimentally testable status of the conclusions explicit. The revised discussion identifies total nuclear active Cyclin B–Cdk1 content and effective system size as controls of wave-back directionality, states that the nuclear enrichment required for complete reversal remains to be tested, and identifies perturbation of actomyosin contractility while monitoring Cdk1/Rho dynamics as one way to probe the role of omitted mechanics. We therefore present the work as a theoretical framework that generates concrete predictions, not as experimentally validated proof of the mechanism. See Discussion section in the revised manuscript.

(2) Adopts previously published models more or less 'as is', without detailed re-evaluation and re-assessment, or without developing them further.

We agree that the individual modules are adopted without substantial re-derivation or extension, and the revised manuscript now mentions this directly. We now discuss the models in the main text, mentioning the Yang and Ferrell / Puls Cdk1 model and the Michaud et al. cortical model, giving the equations and coupling, and then the Methods sections states that parameter values are retained from the original publications. Our aim is not to claim a new formulation of either module, but to analyze what emerges when they are coupled in a common geometry. That analysis yields the front–back asymmetry, geometry-dependent reversal of the Cdk1 wave back, and distinct cortical reactivation regimes. See Introduction, Model, Methods, and Results in the revised manuscript.

Overall, I find this work important, as it shows that combining models of the CDK1 gradient and Rho activation modules can explain the surface contraction waves observed in oocytes. Strikingly, it elegantly explains the differences seen between different experimental systems. While previously these were considered a 'controversy', modeling shows that the differences are simply a consequence of the difference in the size of the oocytes. In addition, the model makes several intriguing predictions that can be tested in future experiments.

We thank the reviewer. In revising the manuscript, we were careful not to reduce the mechanism to cell size alone: the model shows that directionality depends jointly on effective cell size and total nuclear Cdk1 content, which is set by nuclear size and nuclear concentration. We now mention this combination consistently and make the associated predictions explicit in the Discussion. See Results and Discussion in the revised manuscript.

Reviewer #3 (Public review):

Summary:

Using realistic mathematical models, Cebrián-Lacasa et al. address the relationship between waves of activation of Cyclin B-Cdk1 that propagate through the cytoplasm of large (~1 mm) oocytes and fertilized eggs and surface contraction waves (SCWs) driven by Rho GTPase activity in the cell cortex. They present numerical simulations of the underlying reaction-diffusion equations that account in broad strokes for both the expected behavior of 'fronts' of Cdk1 activation (that propagate at constant velocity from the nucleus-the source of Cdk1 activity-to the cell cortex) and the unusual behavior of 'backs' of Cdk1 inactivation (that may propagate either away from or towards the nucleus, or exhibit simultaneous inactivation throughout the cytoplasm). They also model Rho GTPase activity in the cortex as an excitable system that propagates SCWs (target patterns, spiral waves, and more complicated patterns). When Cdk1 is activated in the cortex, it phosphorylates and inhibits the RhoGEF, Ect1, which suppresses SCWs by reducing Rho GTPase activity. As the wave-back of Cdk1 inactivation moves across the cortex, Rho GTPase activity recovers abruptly, and SCWs reappear as 'phase waves' whose speed and directionality are determined by the underlying cytoplasmic Cdk1 signal.

Strengths:

As a theoretical examination of an interesting and puzzling aspect of early embryonic development, this study shares the same strengths and weaknesses as all mathematical and computational approaches to molecular cell biology. The mathematical models are precise formulations of the underlying assumptions of the authors (which are quite reasonable in this reviewer's opinion), and the analysis and computational results are dependable consequences of the molecular mechanisms the authors have in mind. The model is expertly analyzed, and the results are both reliable and intriguing. The results are discussed in light of experimental evidence. Because the authors' methods and results suggest novel-and sometimes counterintuitive-avenues for experimental research, this paper is likely to have a significant impact on the field of Rho GTPase signaling in oocytes and early embryos, and perhaps in other cells as well.

We thank the reviewer for this thoughtful assessment. We have preserved the mathematical formulations and made the assumptions, mechanisms, and experimentally testable consequences easier to identify. In particular, the revised Results section emphasizes the distinct mechanisms governing the activation front and wave back, the revised figures provide a more intuitive visual explanation, and the Discussion separates experimentally supported observations from model predictions. See Model, Results, and Discussion in the revised manuscript.

Weaknesses:

Like all mathematical models, the underlying assumptions can be critiqued as neglecting this -or-that 'crucial' effect (e.g., mechanical coupling via cortical tension or cytoplasmic flow, as the authors acknowledge), and the highly technical methods of analysis and simulation can be unfamiliar and off-putting to experimental cell biologists. The paper is a difficult read, even for an experienced theoretician. For those who take the time to understand this paper, it may change the way they think about the coupling of cell cycle control (Cdk1 activation and inactivation) and cell surface contraction waves.

We agree on both accessibility and model scope. To improve accessibility, we added the core equations and parameters to the main text, introduced more qualitative descriptions of the dynamical regimes, and redesigned Fig. 2B to show the physical mechanism schematically. We also expanded the discussion of the limitations. We did not add mechanical coupling to the model in this revision; instead, the manuscript now states explicitly that showing biochemical signaling to be sufficient within the model does not demonstrate that cortical tension, cytoplasmic flow, or surface deformation are unnecessary in living cells. These effects are identified as additional important factors that can affect the dynamics and as targets for future perturbation experiments. See Model, Results, Fig. 2B and caption (p. 6), Discussion in the revised manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Carefully proofread the manuscript, Figures, and Figure Legends to make sure that statements are accurate. Please describe in more detail what is shown in every Figure panel. The units of diffusion in Figure 2C appear wrong, total activity is not really explained in the text, and it is a strange use, as the activity changes over time; the units of total activity are millimolar, which seems unrealistic. The Figure 1D heatmap does not explain what is plotted. Intensity is neither defined nor is it clear how the first wave front was drawn; the second appears to be convincing. The curvature of what physical object is plotted in Figure 1D, and again, how are the wavefronts on those Figures drawn?

We carefully reviewed the manuscript and all main and supplementary figures. Figure 1 was redesigned to show the model in 3D, 2D, and 1D and to make the coordinates used in the kymographs explicit. The revised Fig. 1 caption now states that the experimental color scales correspond to Cdk1-reporter intensity (top) and local membrane curvature (bottom), and that the dotted lines mark the tracked front and back. These overlays are intended as visual guides in the adapted experimental kymographs rather than quantitative fits used in our model analysis. Figure 2 was also redesigned and its caption expanded. The diffusion coefficient is now reported in μm²/s. In addition, we identified and corrected an error in the conversion of total active nuclear Cyclin B–Cdk1. The corrected control variable is total active nuclear content, reported in pmol and defined explicitly in Eq. 7; the affected main and supplementary plots were regenerated. See Fig. 1D and Fig. 1 caption (p. 3); Fig. 2 and caption (p. 6); Results, Methods, Eq. 7, Table 1 (p. 16) and Supplementary Figs. S3–S4 in the revised manuscript.

(2) Provide a better intuitive explanation of the proposed mechanism.

We substantially rewrote the Results section describing geometry-controlled directionality. The revised explanation first establishes the front–back asymmetry and then gives an intuitive description: a constant-speed activation front coexists with a slower diffusive spread of the elevated nuclear pool; because diffusion lags behind the front, distant regions can relax earlier, creating a gradient that drives an inward wave back. Revised Fig. 2B depicts these processes schematically. See Results, especially Fig. 2B and caption (p. 6) and Discussion in the revised manuscript.

(3) Reduce claims of novelty when not justified. I think that there is a potentially interesting idea in this paper, but also a lot of known facts that are revisited, and being unclear about what was known and what is new does not help the manuscript.

We agree. The revised Abstract and Introduction sections explicitly say that we couple established models rather than develop new individual modules. The Model section cites the original sources of each module, and the Introduction distinguishes established biological coupling from the question addressed here. We reserve the main contribution for the consequences of the coupled analysis: front–back asymmetry, the joint control by nuclear Cdk1 content and effective system size, and the resulting cortical response. The discussion also mentions the key unvalidated step as a testable prediction. See Abstract, Introduction, Model and Discussion in the revised manuscript.

(4) The interface of Cdk1 activity with actomyosin contractility (and cortical dynamics) is much better understood in other systems, and discussing those systems will improve the impact of the paper.

We expanded the Introduction to include Drosophila and zebrafish and to note the established functions of Cdk1-controlled actomyosin dynamics in nuclear positioning and ooplasmic segregation. This broader context makes clear that Cdk1–cortex coupling was already established and that our specific question is how cytoplasmic wave geometry shapes the downstream cortical response in large oocytes and eggs. See Introduction section in the revised manuscript.

(5) Be clearer about what the goal of this paper is and keep the focus on that. In my opinion, there is too much writing spent describing known facts.

We revised the Introduction to move more directly from the biological puzzle to the central question and then into the coupled model. The manuscript now explicitly states that we ask whether the opposite SCW directionality can follow from geometry and nuclear Cdk1 content rather than organism-specific cortical mechanisms, and then ask how the resulting cytoplasmic waveforms are transmitted to the cortex through Ect2 inhibition. We also reduced repeated background material and moved the core mathematical specification into a dedicated Model section. See Introduction, Model and Results in the revised manuscript.

(6) A discussion that the Cdk1 spatiotemporal patterns remain to be analyzed in both Xenopus and starfish embryos would be appropriate.

We added this limitation to the discussion in a way that distinguishes what is known from what remains to be measured. The revised text summarizes observations supporting nuclear enrichment and wave initiation but also says that whether nuclear active Cyclin B–Cdk1 reaches the levels required for complete wave-back reversal remains experimentally to be tested. We also avoid presenting the starfish intracellular Cdk1 wave as established fact. See Introduction, Results, and Discussion in the revised manuscript.

Reviewer #2 (Recommendations for the authors):

(1) I have one main suggestion. I would find it important that the authors present the models in more detail in the main text. In principle, even if they adopted previously published models, the reader should not need to go back to those original papers to find the equations and parameters. Readers should not even need to dig deep into the supplemental material. For example, the main equation used to model the CDK1 gradient should be shown in the main text with critical parameter values listed. For example, the text mentions that the diffusion coefficient of CDK1-Cyclin B has a critical importance (which I very much agree with), but I could not easily find the values used and still had to guess the units.

We agree. We added a dedicated model section to the main text containing the governing reaction-diffusion equations for both modules and the Cdk1–Ect2 coupling. The variables and roles of the principal parameters are defined there, while Table 1 lists the standard parameter values and units, including the diffusion coefficients used for the cytoplasmic regimes. The total active nuclear Cyclin B–Cdk1 control variable is defined explicitly in Eq. 7 in the Methods section. See Model, Methods, Table 1 (p. 16) and Eq. 7 in the revised manuscript.

(2) Overall, the manuscript is well written and nicely illustrated. However, the text could be more concise and, as explained above, show more equations rather than trying to describe them in words. Some of the illustrations could also be larger and possibly shown at higher contrast. Finally, the subtitles could be more imaginative, describing the main finding rather than simply stating what has been done.

We revised the manuscript throughout to reduce repeated background material and to replace lengthy verbal descriptions of the core model with equations in the main text. We standardized figure text and redesigned several panels, especially Figs. 1 and 2, to improve readability and interpretability. We did not replace every subsection title, but we have tried to use clear descriptive titles (with a message where possible). We revised several headings in the Results section so that they communicate the main finding directly, for example “Front–back asymmetry: traveling fronts and gradient-controlled backs,” “System size and diffusion modulate gradient effectiveness,” and “Phase diagram of Cdk1 waves.” See Introduction, Model, Results headings and text, Figs. 1– 2 and captions; supplementary figures in the revised manuscript.

(3) The starfish work focuses on meiosis I, not meiosis II.

We reviewed the stage-specific wording throughout. Rather than replacing every reference with “meiosis I,” we removed unnecessary stage labels where the argument concerns starfish oocyte meiosis more generally, and we use stage-specific wording only when it is supported by the cited experiment. In particular, Fig. 1 now labels the experimental panel simply as starfish meiosis rather than meiosis II. See Fig. 1D and caption (p. 3); Introduction and Results in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

(1) Figure 1D. Right: experimental kymographs. What are 'intensity' and 'curvature'? I suppose 'intensity' refers to Cdk1 activity and 'curvature' to local curvature of the cell membrane. If so, Cdk1 activity seems to propagate as a wave around the cortex from the animal pole, but (I suppose) these are phase waves rather than trigger waves, because the nucleus is closer to the animal pole, so the cytoplasmic trigger waves reach the cortex sooner there and later at larger values of phi. In the starfish oocyte, the curvature 'bumps' at the animal pole and the equator seem to be stationary. Maybe I am misinterpreting the data; in any case, it might help readers to guide their reading of this data.

We clarified both the labels and the interpretation. The revised Fig. 1 caption explains the plotted experimental quantities as Cdk1-reporter intensity (top) and local membrane curvature (bottom), and mentions that the dotted lines mark the tracked front and back. We also distinguish the cytoplasmic propagation from the cortical phase-wave readout. Because the nucleus is off-center, the distance from the nuclear source to the cortex varies with angular position, so the radial Cdk1 solution is sampled at different times around the cortex. The Numerical methods now state explicitly that this geometry produces the angle-dependent arrival times shown in Fig. 1D. See Fig. 1D and Fig. 1 caption (p. 3); Model geometry and Numerical methods in the revised manuscript.

(2A) In panels (ii) and (iii), what is the meaning of the hyperbolic dotted line labelled 'underlying diffusion'?

The original schematic was replaced by the reworked Fig. 2B. The revised schematic and results now separate the outward trigger-wave-like front from the slower diffusive spread of the elevated nuclear pool. The “underlying diffusion” component is therefore no longer an unexplained fitted-looking curve; it is presented as the diffusive process that establishes the gradient controlling the wave back. See Fig. 2B and caption (p. 6) and Results in the revised manuscript.

(2B) This panel is very confusing. What is the significance of all the different colored lines? What is the meaning of '◄Time'? This panel needs more explanation. Also, fix 'increaseded'.

We agree that this was confusing. We now redrew Fig. 2B as a two-dimensional schematic with a consistent activity color scale and explicit labels for the phases and dynamical processes. The ambiguous time-arrow presentation was removed, and the typographical error was corrected. See Fig. 2B and caption (p. 6) and Results in the revised manuscript.

(2C) Units of diffusion constant are wrong; should be μm2/s. Also, please explain (perhaps in context of Figure S3) how you calculate 'units of active nuclear CycB-Cdk1 (mmol)' in terms of total [CycB-Cdk1] in the nucleus, radius of the nucleus, and model parameter γ.

The diffusion coefficient is now reported consistently in μm²/s. We also identified and corrected an error in the conversion to total nuclear amount. Eq. 7 now defines the total active nuclear Cyclin B–Cdk1 content from the enriched nuclear active concentration and nuclear volume; γ scales the nuclear concentration relative to the cytoplasmic baseline. The corrected quantity is reported in pmol, not mmol, and the corresponding main and supplementary plots were regenerated. Supplementary Fig. S3 shows that varying γ or nuclear radius collapses onto this single control variable. See Fig. 2D and caption (p. 6); Results, Methods, (Eq. 7), Table 1 (p. 16) and Supplementary Fig. S3 in the revised manuscript.

(2D) Please explicitly indicate the speed of the wave front, because it is difficult to read, given the scale of the vertical axis.

Agreed. The revised Fig. 2 caption now explicitly states that the wave-front velocities are fitted by a quasiconstant velocity of approximately 23 μm/min. See Fig. 2D caption (p. 6) and Results in the revised manuscript.

(3) Box 2. C. You might indicate that the Rho-actin dynamics are oscillatory for 0.59 < α < 1.02 and excitable for α slightly larger than 1.02 and (I suppose) slightly smaller than 0.59. Furthermore, I suppose (given the results in Figure 4) that the system does not propagate waves for α {less than or equal to} 0.5. Somehow, the authors should indicate how wave propagation is suppressed for small values of α.

We clarified the bifurcation structure and the low-α suppression of cortical activity. We did not adopt the proposed regime labels verbatim, because the spatial model supports propagating waves across a broader active window than the homogeneous oscillatory interval alone would suggest. The revised text therefore reports the two Hopf bifurcations at α = 0.59 and α = 1.02, states directly that the cortex is quiescent for low α, and reports that propagating waves persist across 0.59 < α < 1.26 up to the wave instability at α = 1.26. This directly explains how sufficiently strong Cdk1-mediated reduction of effective Ect2 suppresses propagation. See Box 2C (p. 9) and Results in the revised manuscript.

(4) Lines 273 and 294. "These differences arise...".

Corrected. The relevant Results text was rewritten during the broader restructuring, so the original wording no longer appears. See Revised Results.

(5) Lines 380, 381. "...the Hopf bifurcation (at α = 0.59) that separates...".

We did not retain the sentence in its original form. Instead, the revised text now identifies both Hopf bifurcations explicitly (α = 0.59 and α = 1.02), states the wave-propagating window, and then describes how Cdk1derived inhibition moves the cortical system across the bifurcation during suppression and recovery. We believe this is clearer than adding the parenthetical phrase to the old sentence. See Results and Box 2C (p. 9) in the revised manuscript.

(6) Table 1. Include a value for α_0.

Done. Table 1 now lists α₀ = 1 (dimensionless), and the Methods state that α = α₀ = 1 before nuclear envelope breakdown. See Table 1 (p. 16) and Methods in the revised manuscript.

(7) Line 522. What does 'implemented manually' mean?

We replaced the ambiguous wording. The Numerical methods now state that both models were integrated with an explicit second-order Runge–Kutta method implemented in custom code; the cytoplasmic and two dimensional cortical simulations use finite differences, and the three-dimensional cortical simulations use a finite element method implemented in FEniCSx. See Numerical methods in the revised manuscript.

(8) Figure S1. A. The first green dot should be labelled γ = 1. B. Left panel is γ = 1, I suppose.

Corrected. Revised Supplementary Fig. S1 explicitly labels the baseline γ = 1 condition and the enriched γ = 1.5 condition. Its caption also explains that γ scales the nuclear concentration above the cytoplasmic baseline while preserving the active-to-total ratio. See Supplementary Fig. S1 and caption; Model in the revised manuscript.

(9) Figure S2. What is X_0? How is it related to γ?

We addressed this by removing the X₀ notation rather than adding another conversion. The revised supplementary analysis uses γ directly as the nuclear enrichment factor, defined in the main Model section and illustrated in Supplementary Fig. S1. The revised Supplementary Fig. S2 now focuses on the fitted wave-front and wave-back trajectories for different γ values. See Model, lines 123–132; Supplementary Figs. S1–S2; Methods, lines 620–638.

(10) References. Emphasis is on post-2010 literature. One classic paper on SCWs is mentioned: Hara (1971). The classic publication on Cdk1-driven mitotic waves in fruit fly embryos is Foe & Alberts (1983) J Cell Sci 61:31. The first theoretical prediction of Cdk1 trigger waves in syncytial cells was given by Novak & Tyson (1993) J Theor Biol 165:101. Citing Deneke et al. (2016) Dev Cell 38(4) could also be considered.

We added the suggested literature. Novak & Tyson (1993) is now cited for the early theoretical prediction of trigger-wave behavior; Foe & Alberts (1983) is cited in the discussion of cell-cycle/cortical waves; and Deneke et al. (2016) is cited in the Introduction both in the mitotic-wave context and in the broader discussion of Cdk1–actomyosin coupling. See Introduction and reference list in the revised manuscript.

Author response:

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

eLife Assessment:

Using genome databases, the authors performed solid bioinformatic analyses to trace the genomic history of the clinically relevant Staphylococcus aureus tetracycline resistance plasmid pT181 over the last seven decades. They discovered that this element has transitioned from a multicopy plasmid to a chromosomally integrated element, and the work represents a valuable demonstration of the use of publicly available data to investigate plasmid biology and inform clinical epidemiology. This work will appeal to researchers interested in staphylococcal evolution and plasmid biology.

Thank you, we agree with this overview. We also think this work is interesting to people interested in antimicrobial resistance and bacterial genome structure.

Public Reviews:

Reviewer #1 (Public review):

The study provides a robust bioinformatic characterization of the evolution of pT181. My main criticism of the work is the lack of experimental validation for the hypotheses proposed by the authors.

Comments on the study:

(1) One potential reason for the decline in pT181 copy number over time may be a high cost associated with the multicopy state. In this sense, it would be interesting if the authors could use (or construct) isogenic strains differing only in the state of the plasmid (multicopy/integrated). With this system, the authors could measure the fitness of the strains in the presence and absence of tetracycline, and they could be able to understand the benefit associated with the plasmid transition. The authors discuss these ideas, but it would be nice to test them.

We agree that the relative fitness of integrated versus multicopy plasmids is interesting and a costly multicopy state could explain the transition of independent pT181 replicons to chromosomal integration. This is a project we are exploring for a future study. However, we think that this additional experimental work goes beyond the scope of the paper.

(2) It would be interesting to know the transfer frequencies of the multicopy mobilizable pT181 plasmid, compared to the transfer frequency of the plasmid integrated into the SSCmec element (which can be co-transferred, integrated in conjugative plasmids, or by transduction).

We agree with the reviewer that this is an interesting question. However, we think inferring these rates from natural sequence data is not feasible in this case given the low heterogeneity of the plasmid sequence. A laboratory-based experimental study could not address the real transfers we observe over the course of decades, as in vitro S. aureus transfer rates are often not good proxies for in vivo (McCarthy et al.). In addition, we do not know what is moving the integrated plasmid. pT181 could be moved by a phage or plasmid, so we are uncertain what the correct experiment would be to explore this.

(3) One important limitation of the study that should be mentioned is that inferring pT181 PCN from whole genome data can be problematic. For example, some DNA extraction methods may underestimate the copy number of small plasmids because the small, circular plasmids are preferentially depleted during the process (see, for example, https://www.nature.com/articles/srep28063).

We have further investigated the role of technical variation in influencing measured PCN. The decline in copy number over time within our longest-collected strain remains significant after controlling for a number of technical variables: instrument used, type of DNA extraction technique, and sequencing center. In addition, plasmid copy number estimations between extraction techniques are not significant when comparing contemporaneously collected samples. We have added these supporting analyses to our results (L328-333) and methods (L612-634).

Reviewer #2 (Public review):

Summary:

The authors performed bioinformatic analyses to trace the genomic history of the clinically relevant pT181 plasmid. Specifically, they:

(1) tracked the presence of pT181 across different S. aureus strain backgrounds through time. It was first found in one, later multiple strains, though this may reflect changes in sampling over time.

(2) estimated the mutation rate of the chromosome and plasmid.

(3) estimated the plasmid copy number of pT181, and found that it decreased over time. The latter was supported by two sets of statistical analyses, first showing that the number of single-copy isolates increased over time, and second, that the multicopy isolates demonstrated a lower PCN over time.

(4) reported the different integration sites at which pT181 integrated into the genome.

As a caveat, they mentioned that identical plasmid sequences have variable plasmid copy numbers across different genomes in their dataset.

Strengths:

This is a very solid, well-considered bioinformatic study on publicly available data. I greatly appreciate the thoughtful approach the authors have taken to their subject matter, neither over- nor underselling their results. It is a strength that the authors focussed on a single plasmid in a single bacterial species, as it allowed them to take into account unique knowledge about the biology of this system and really dive deep into the evolution of this specific plasmid. It makes for a compelling case study. At the same time, I think the introduction and discussion can be strengthened to demonstrate what lessons might be drawn from this case study for other plasmids.

Weaknesses:

The finding that the pT181 copy number declined over time is the most interesting claim of the paper to me, and not something that I have seen done before. While the authors have looked at some confounders in this analysis, I think this could be strengthened further in a revision.

We have investigated this issue further in revisions. The decline in copy number over time within our longest-collected strain remains significant after controlling for a number of technical variables. In addition, plasmid copy number estimations between extraction techniques are not significant. We have mentioned these updates in the results (L327-333) and provided more explanation for the extraction technique in the methods (L612 - 634).

For the flow of the storyline, I also think the estimation of mutation rates (starting L181) and integration into the chromosome (starting L255) could be moved to the supplement or a later position in the main text.

We have chosen to keep the structure of the results largely the same.

Clearly, the use of publicly available data prevents the authors from controlling the growth and sequencing conditions of the isolates. It is striking that they observe a clear signal in spite of this, but I would have loved to see more discussion of the metadata that came with the publicly available sequences and even more use of that metadata to control for confounding.

We have further investigated the role of technical variation in influencing measured PCN. The decline in copy number over time within our longest-collected strain remains significant after controlling for a number of technical variables: instrument used, type of DNA extraction technique, and sequencing center. In addition, plasmid copy number estimations between extraction techniques are not significant when comparing contemporaneously collected samples. We have added this to our results section (L327-333) and explain further in the methods (L612 - 634). Unfortunately, the metadata is incomplete for many isolates, limiting our ability to control for other possible confounders.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I would recommend doing some experiments to test the fitness effects of pT181 in multicopy and integrated into an isogenic S. aureus strain. Simple growth curves with and without tetracycline would be extremely informative.

We think that this is an interesting scientific question but is beyond the scope of this paper.

Reviewer #2 (Recommendations for the authors):

Major:

(1) L160 and Figure 1:

To what extent is this decrease in pT181 prevalence related to a delay between isolate collection and sequence upload to public databases? In my own work, I have found an average of 2 years difference in the sequence collection and sequence upload date of GenBank sequences. This could explain the decreasing numbers in recent years and may possibly skew relative proportions of pT181 containing/or plasmid-free strains.

There are fluctuations in collection rates over the years which definitely do not correspond to actual fluctuations in S. aureus prevalence in the population. We would expect delays in uploads in both plasmid-containing and plasmid-free strains, so we would not anticipate a decline in estimated plasmid prevalence due to this delay; however, it could be somewhat noisy for more recent years.

The large peak of S99.5_27 around 2009 seems oddly reminiscent of targeted sampling during a hospital outbreak, or so? Did you do any checks on where these genomes came from? Could this affect any of the downstream results?

The 2008 peak in S99.5_27 comes from a single BioProject (PRJEB4140), which contributed approximately 1,000 samples to our analysis. Based on the BioProject description, this BioProject aimed to characterize diversity in S. aureus ST239 diversity in Thailand. We performed the single-copy analysis with this strain excluded and still got the same result that integration has increased over time, so we feel that this is acceptable and should not unduly impact downstream results. We have clarified the results section to more explicitly state that this is the sampling peak that was excluded (L306-311).

(2) Figure 3: If I understand the analysis correctly, all mutation rate and phylogenetic analyses were conducted based on comparison to a single reference genome. This can bias results: https://academic.oup.com/mbe/article/31/5/1077/2925634 . Please comment.

Yes, SNPs were calculated relative to a reference genome. We understand this could bias results. However, it is standard practice in the field and we do not think it changes the main findings of the paper.

We have taken the reference-free SKA alignment and the SKA alignment mapping to a reference plasmid and calculated the SNP distances between all plasmid pairs with the tool snp-dists (Seemann et al.). For given plasmid pairs, the distributions are different by Wilcoxon signed-rank test with continuity correction (p < 2.2 x 10^-16) though this is due in part to the large sample size for pairwise comparison. The median and modal difference between methods is 0 SNPs detected. The average is 0.1 more SNPs detected in the reference-free method than the mapping method. We have added this analysis to the methods section (L505-511).

(3) I am not fully convinced by the analysis in Figure 6 (i.e. that the pT181 copy number has declined over time). It is rather confusing how the authors account for strain and bioproject-related influences on their primary regression (L298-306).

We have edited the explanation of the GLMM in the results section (L320-323). We have moved some of the explanation to the methods section (L592-605).

(a) What does this analysis look like without S99.5.2?

The slope is still negative and significant with S99.5_2 excluded. We have added this to the results (L327-328).

(b) In line 296, it is made clear that 2 separate analyses were carried out, but in the subsequent paragraphs (starting 298 and 315), it would be helpful to repeat that each looks at only one component.

We have edited this section to explicitly state that separate regressions were carried out for each component (L298-300).

(c) Figure 6 should include error bars that reflect the different number of samples per collection year (please also comment on how this influences the power/validity of the linear regression!).

We have modified Fig. 6A to show samples collected per year as the color of the point. Samples collected per year can also be viewed in Fig. 1. In addition, we have changed to logistic regression to assess single-copyness as a function of collection year. The error bar on the regression curve shows the SE range. While there are many more samples collected in recent times than in the more distant past, we still think the signal is real. It does put more emphasis on each early sample. However, the genomic data matches early descriptions of tetracycline resistance in S. aureus being plasmid-mediated, not chromosomal (Gillespie et al.).

(4) Strains that were isolated in the 60s were presumably sequenced at a much later point in time. Were they grown and isolated from their respective host bacteria following similar protocols as present-day isolates? Growth conditions can have massive effects on PCN, and selective PCR amplification on the relative number of plasmid-related reads. How do you account for this? [Figure 7/8].

Yes, samples that were collected in the 1960s were sequenced roughly 50 years later. The date of collection could impact storage conditions for the isolate. However, they were grown up for sequencing and actually sequenced much closer together and should have the same growth conditions as isolates collected at a more recent date. Underlying our model of PCN is that it is a property of the isolate and will not fluctuate over time in storage.

Minor:

(1) This study is a nice demonstration of the type of genomic epidemiology that can be conducted now that genomes are sequenced and shared more widely. This is already somewhat common for clinically relevant sequence types of pathogenic bacteria, but I have not seen it much for plasmids. This could be nice to highlight. Stressing this more clearly in the abstract and introduction may broaden the audience of this work.

We have described our approach as genomic epidemiology in the first paragraph of the introduction (L72).

(2) More generally, the introduction is quite winding. A lot of interesting information is mentioned, but without a clear narrative structure as to why this is important for the study. Some editing may strengthen the message of the paper and invite more people to read it. For instance, starting each paragraph with a topical sentence about the general message the paragraph should convey. Yet, this is entirely a style/personal taste remark, and I leave it to the authors to decide whether to make these changes.

We have made edits to restructure the text.

(2a) Similar comment for the discussion (possibly some discussion could be put in the supplement too).

We have made edits to restructure the text, but have chosen to leave the content in the Discussion section. Additional references to previous research have also been added (L386-388).

(3) L125: Could you include a reference for this statement?

We have added a reference for this statement (L109).

There is interesting existing work on the evolution of genes on multi-copy plasmids (and the evolution of copy-number itself), which seems more pertinent here than the segregation mechanisms of low-copy-number plasmids.

We have chosen to keep the general background on plasmid copy number regulation and segregation, to keep the paper approachable to readers who have no background on plasmid biology. We have added additional references to work on evolvability of multicopy plasmids and their copy number (L117-120).

(4) The references are a bit of a mess. Certain entries are in all caps, others are missing titles, etc. I would recommend looking this over again carefully.

We have resolved this issue.

(5) L187 CDS is used in line 187 but not defined as a term until line 201.

We have defined CDS with first usage (L188).

(6) L189: Do you have any estimate of the error around 1.15 mutations/Mb/year from the linear regression?

We have added standard error for the 1.15 mut/Mbp/year from the regression to the results (L191): SE = 0.3 mut/Mbp/year.

(7) Figure 2: It would be helpful to have a visual indication of which areas the authors consider hypervariable.

We have added a black dash underneath the hypervariable regions on the plot.

(8) Figure 5: The two colors of grey are hard to distinguish.

The grey for shared genes has been made darker to better distinguish them.

(9) L285: Why do you write "could assume the copy number of the larger element"? What other options are possible?

We have expanded on this section to elaborate on the ways that copy number could be changed by cointegration, and added an additional citation to support these claims (L276-280).

(10) Figure S1: What does this scale mean? What are the units? This figure is uninformative as it stands. I would possibly consider labelling the tips.

We have modified the figure and legend to indicate that the scale is in substitutions per site. We are providing these figures to give some idea of scale and shape, showing how star-like they are. Unfortunately, tip labels are illegible on these trees given the large number of samples.

References

Gillespie, M. T., et al. “Antibiotic Susceptibilities and Plasmid Profiles of Nosocomial Methicillin-Resistant Staphylococcus aureus: A Retrospective Study.” Journal of Medical Microbiology, vol. 17, no. 3, June 1984, pp. 295–310. DOI.org (Crossref), https://doi.org/10.1099/00222615-17-3-295.

McCarthy, Alex J., et al. “Extensive Horizontal Gene Transfer during Staphylococcus aureus Co-Colonization in Vivo.” Genome Biology and Evolution, vol. 6, no. 10, 2014, pp. 2697–708, https://doi.org/10.1093/gbe/evu214.

Seemann, Torsten, et al. Snp-Dists. https://github.com/tseemann/snp-dists.

Author response:

Reviewer #1 (Public review):

Summary:

This manuscript reports exceptionally preserved, millimeter-scale segmented bilaterian microfossils from the Fortunian Kuanchuanpu Formation in South China. The authors propose that these non-biomineralized animals were preserved through microbial pseudomorphs rather than direct phosphatization, filling a critical taphonomic and evolutionary gap in early animal segmentation.

Strengths:

This paper filled the critical taphonomic and evolutionary gap in early animal segmentation.

Weaknesses:

Extremely similar work has already been published by Xian et al., 2026, PNAS, with specimens from absolutely the same formation, and they also proposed that these animals are segmented. So in this context, this work's significance is eclipsed.

Thanks the reviewer for the constructive comments. In Xian et al., 2026, PNAS, the taphonomic mechanism has not been explained in details and in our manuscript we propose the mode that how microbes pseudomorph the entire bodies of micro-animals. In addition, the specimens we presented in this manuscript demonstrate the abundance and diversity of segmented bilaterians in the basal Cambrian. In the revision, we will majorly discuss the evolution of body segment based on our new materials and add a new figure to complement the comparison of microbial pseudomorphs vs Ediacaran-type and Burges-Shale type.

Reviewer #2 (Public review):

Summary:

The manuscript by Yang and authors presents an interesting set of new microfossils from the early Cambrian of South China. These are interpreted as segmented bilaterians, and so may be the oldest such examples in the fossil record, with implications for our understanding of early animal evolution. Further, the preservation of these fossils as microbial pseudomorphs is a unique pathway to fossilize such important organisms.

Strengths:

The fossils are impressive and arguments for their affinities as segmented bilaterians are convincing. Discussion of somewhat novel preservation is detailed and helpful to understand this taphonomic mode.

Weaknesses:

It needs to be clear what the authors' definition of a "segment" is and how that matches (or not) other interpretations. Arguments by Hannibal and Patel (2013, EvoDevo) convincingly define all segmented organisms based on polarity within repeated units of bilaterally symmetrical animals, but others may disagree. The manuscript would benefit from discussion of this in the introduction, laying out a hypothesis for what we might expect to find as evidence of the earliest segmented animals and then describing these new fossils within that context.

As it currently reads, the definition of a segment is not presented until the discussion and is somewhat ambiguous, seemingly referring to any organism with bilateral symmetry and repeated units. However, modern (e.g. tardigrades) non-segmented animals exhibit these features but are not considered truly segmented. This is critical as various Precambrian fossils (Arborea (Dunn et al., 2019, Palaeontology); Cloudina (Schiffbauer et al., 2020, Nature Communications) Dickinsonia (Gold et al., 2015, Evolution and Development); Parvancorina (Darroch et al., 2017, Biology Letters); Spriggina (Evans et al., 2026, Scientific Reports); Yilingia (Chen et al., 2019, Nature) etc.), have been argued to possess bilateral symmetry ad have bodies composed of repeated units. These older examples should be acknowledged and discussed in detail. Stating that "the identity of these [Precambrian] organisms is controversial" (line 51) is not justification for the main claims of this paper, and it should be clear what distinguishes the new fossils from previously proposed evidence of earlier segmented bilaterians. I believe there is a case to be made in support of the authors' claims, but this context is vital to make that argument convincingly. It is also worth discussing evidence of segmented bilaterians in the early Cambrian trace fossil record, such as Treptichnus pedum (Kesidis et al., 2019, Proceedings B) and Rusophycus (Daley et al., 2018 PNAS), that may predate or be roughly coeval with these fossil remains.

Thanks for the valuable suggestions and references from the reviewer. In the revision, we will introduce the definition of segment and former researches in the introduction part as suggested. And we will discuss the comparisons of our specimens with the Precambrian fossils mentioned above in more detail. The major difference between our materials and Spriggina and Yilingia is the undisputed bilateral symmetry. While the paired appendages distinguished the Cambrian fossils from Parvancorina, Cloudina, and Dickinsonia. Since the pseudomorphing mechanism caused the lost of internal structures of the original, the well-developed paired appendages and outer segment could be the major evidence of their identity. In addition, we will make a more detailed introduction and discussion on the trace fossils of during the Ediacaran-Cambrian transition.

Author response:

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

eLife Assessment

This valuable study compares hippocampal-cortical functional connectivity to various other brain measures and examines their development across youth. It uses sophisticated analyses replicated in multiple datasets, but provides incomplete evidence to support the primary claim that hippocampal-cortical connectivity relates to cognitive maturation. The manuscript would benefit from a more nuanced consideration of the biological basis of some of the derived imaging measures and the limitations of the cross-sectional design. This work will be of interest to neuroimaging specialists and cognitive neuroscientists.

We thank the Editors for credits on the value of the multimodal, multi-dataset design and the study’s relevance to cognitive neuroscience. We have revised the manuscript in three corresponding ways:

(1) Connectivity–cognition interpretation. We now state explicitly that the hippocampal-cortical connectivity–cognition findings are age-related associations with cognitive measures during youth. They do not demonstrate that hippocampal-cortical connectivity causes, mediates, or fully explains cognitive maturation.

(2) Biological interpretation of imaging measures. We refined the interpretation of derived imaging measures throughout the manuscript. T1w/T2w is described as an indirect, myelin-sensitive but non-specific MRI contrast that may reflect multiple tissue and acquisition factors, rather than direct myelin content. Similarly, transcriptomic findings are described as cross-dataset spatial associations rather than evidence of developmental molecular mechanisms. Consistent with recent guidance on neuroimaging data contextualization, the interpretation of these associations is constrained by the characteristics of the reference atlas and by cross-dataset spatial alignment[1].

(3) Limits of cross-sectional evidence. We added an explicit limitation that the cross-sectional design does not measure within-person developmental change and cannot establish temporal ordering or causal relationships.

Together, these revisions address the evidential limitations identified in the Assessment while preserving the supported contribution of the replicated multimodal associations.

Reviewer #1 (Public Review):

Summary:

The authors studied the development of hippocampal connectivity gradients based on open datasets and performed correlation analyses with other MRI features as well as gene expression information from other datasets. Although the main findings are correlational and cross-sectional, the analyses are overall sophisticated and replicated in several datasets.

Strengths:

The hippocampus is a key region in understanding large-scale brain organization and cognition, and the authors applied advanced and suitable analytics to study its development. The paper is overall well-organized and well-written, and the findings are relevant for studying large-scale brain development.

Weaknesses:

While sophisticated, several of the analyses appear mainly correlational, cross-sectional, and rely on cross-dataset contextualization, which should also be stated as a limitation of the current work.

We are grateful to Reviewer #1 for recognizing the importance of the hippocampus, the suitability of the analytical framework, and the value of the replicated developmental design. We agree that the public-review concern about correlational, cross-sectional, and cross-dataset evidence is central to how the findings should be interpreted. In particular, consistent with recent recommendations for neuroimaging data contextualization, we now explicitly identify the transcriptomic component as group-level spatial contextualization and state that its interpretation is limited by the properties of the adult post-mortem reference atlas and by cross-dataset spatial alignment[1]. It therefore cannot provide individual-level developmental inference or establish causal molecular mechanisms. We have addressed these boundaries in detail in our response to Reviewer #1, Recommendation 1, and in the revised Limitations section, so that the same qualification is applied consistently throughout the manuscript.

Revised manuscript text (Page 29-30): “Although key findings were replicated across two independent longitudinal datasets, the primary developmental analyses were cross-sectional and therefore did not measure within-person change. The absence of pubertal hormone measures in the HCP-D dataset also limited assessment of hormonal contributions to the observed age-related associations. The observed patterns should be interpreted as age-related associations rather than individual developmental trajectories or causal developmental mechanisms. T1w/T2w intensity was treated as an indirect, myelin-sensitive MRI proxy influenced by multiple tissue and acquisition factors, not as direct histological myelin content. Transcriptomic results were based on post-mortem samples from a separate dataset and were interpreted as cross-dataset spatial associations rather than developmental mechanisms. More generally, the interpretation of such cross-dataset map correspondence is constrained by the properties and representativeness of the source atlas and by cross-dataset spatial alignment[1]. These limitations motivate future longitudinal, multimodal, and biologically validated studies.”

Reviewer #1 (Recommendations for the Authors):

(1) Some language suggests causality, but the associated findings were mainly derived from correlational analysis. I would suggest verifying the wording and toning down causal terms ('shape', 'impact', 'linked' ...).

We thank the reviewer for identifying this important mismatch between the strength of the wording and the correlational nature of the evidence. We have completed a manuscript-wide terminology review and replaced causal or mechanistic verbs with relational language throughout the Abstract, Introduction, Results, Discussion, and figure captions. We have used terms such as associated with, corresponds to, covaries with, and is consistent with when describing relationships among gradients, geometry, T1w/T2w intensity, transcriptomic measures, and cognition. Stronger terms have been retained only when they describe a mathematical operation or the construction of an analysis, and the revised Discussion now explicitly states that cross-sectional associations do not establish directionality or causation.

(2) Please also provide the following citations when referring to hippunold: https://elifesciences.org/articles/88404 (which describes additional advanced registrations). If the authors have the ability to quickly rerun some processing, then I would recommend a sensitivity analysis based on hippunfold v2, which also provides more homogenous vertex spacing, fewer distortions during unfolding, and some additional improvements.

We thank the reviewer for pointing out the missing registration reference and for recommending a HippUnfold v2 sensitivity analysis. We have added the requested eLife study on surface-based hippocampal registration and have included the relevant surface-generation and registration procedures for our study.

We carefully considered reprocessing the data with HippUnfold v2. The official release notes indicate that v2 includes important changes to surface precision, surface re-tessellation, Laplace coordinate generation, and robustness to topological breaks. These changes could affect surface coordinates and the precise spatial sampling of imaging data. A meaningful v2 sensitivity analysis would therefore require reprocessing the original MRI data and repeating the downstream connectivity, gradient, developmental, cognitive, and cross-dataset analyses. We did not perform this complete reprocessing in the present revision because it would represent a new version-wide analysis rather than a limited sensitivity check.

We did not consider a partial rerun of selected downstream analyses to provide a sufficiently informative or internally consistent test of version sensitivity. Rather than present an incomplete comparison, we retained the original HippUnfold v1.2.1 pipeline, explicitly identified version dependence as a limitation, and removed wording that could imply that the findings are fully insensitive to preprocessing choices.

We appreciate that a preregistered comparison across HippUnfold versions would be valuable in future work, particularly for analyses in which fine-scale surface correspondence or registration precision is the primary scientific focus.

Revised manuscript text (Page 33): “We employed HippUnfold (v1.2.1)[2] (https://hippunfold.readthedocs.io; advanced surface-registration procedures are described by DeKraker et al.[3]), which integrated a deep learning method with a topological constraint strategy.”

(3) Are there changes in motion parameters across developmental time windows/age? Are findings consistent when fMRI motion parameters are regressed out in the statistical models, and do the 3 derived gradients correlate with head motion?

We thank the reviewer for raising this important potential confound. We noted that the original developmental GAMs already included mean framewise displacement (mFD). First, we tested whether head motion changed with age. In the 601 included HCP-D participants, we fitted mFD as the outcome using mFD ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) with REML estimation. mFD showed a robust nonlinear decrease with age (edf = 2.66, F = 125.13, smooth-term p < 2.2 × 10^-16; likelihood-ratio p < 2.97 × 10^-78; Supplementary Fig. 3a). Importantly, the original developmental models for hippocampal gradient statistics already included mFD as a covariate. We therefore directly examined the mFD coefficients from those same 18 models, which used Feature ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD.

After Benjamini–Hochberg correction across the 18 mFD coefficients, mFD was associated with explained variance for lLG (β = −0.0412, SE = 0.0147, FDR q = 0.047) and qLG (β = 0.0280, SE = 0.00818, FDR q = 0.011), but with nocIG feature (all FDR q ≥ 0.101; Supplementary Fig. 3b). Thus, head motion is strongly age-related and is associated with a limited subset of the analyzed gradient-distribution features, supporting its inclusion as a covariate. The developmental effects reported in Figure 2e–f are already estimated after adjustment for mFD; we do not claim that every gradient feature is motion-independent.

Revised manuscript text

(Page 9): “We fit the model with a smooth term for age as a fixed effect; sex, scanning site, and in-scanner head motion (mean framewise displacement, mFD) as linear covariates”

(Page 10): “The age-related mFD trajectory and direct mFD coefficients from the original gradient feature models are shown in Supplementary Fig. 3.”

(4) Did the authors also observe morphological changes in the hippocampus? Are there changes in hippocampal cortical thickness that could explain some of the changes in functional coupling as well?

We thank the reviewer for this important suggestion. We performed additional HippUnfold surface-morphology analyses and a thickness-adjusted reanalysis of the same gradient features examined in Figure 2 and Extended Data Fig. 4. Morphological measures were calculated separately for each hemisphere after pooling the hippocampal-proper (label-hipp) and dentate-gyrus (label-dentate) surfaces. Thickness, curvature, and gyrification were native-surface-area-weighted, surface area was summed across both labels, and left-hemisphere curvature was sign-oriented to match the right-hemisphere convention.

For each morphology measure, we fitted Metric ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) in 601 included participants, using the same GAM framework as the primary gradient-feature analyses but without mFD. Thickness, oriented curvature, gyrification, and surface area all showed age-related change after FDR correction (all q ≤ 0.000304). Hippocampal thickness decreased from childhood through adolescence and then plateaued, whereas surface area and gyrification increased before reaching late-adolescent plateaus.

To test whether morphology accounted for the functional findings, we refitted each of the 18 original gradient feature models with hemisphere-matched thickness added: Feature ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD + thickness. No individual thickness coefficient survived FDR correction across the 18 features (minimum q = 0.061). Thus, developmental changes in hippocampal and dentate morphology are present, but surface thickness does not account for the principal age-related functional gradient effects.

Revised manuscript text (Page 10):

“Given the age-related variation in hippocampal functional-gradient features, we next assessed whether concurrent changes in global hippocampal morphology could account for these patterns. Surface-area-weighted thickness, curvature, gyrification, and surface area of the pooled hippocampal proper and dentate gyrus showed significant age-related associations (Supplementary Fig. 5). However, after adding hemisphere-matched thickness to the corresponding hippocampal gradient feature models, no thickness association survived FDR correction (minimum q = 0.061). Thus, although global hippocampal morphology changes across youth, these results do not support global thickness as an explanation for the primary functional-gradient patterns.”

(5) The authors corrected for sex in several of their models. It would be interesting to show, in a supplemental form, sex-disaggregated analyses that outline the consistency and/or potential shifts in developmental patterns in males and females.

We thank the reviewer for this valuable suggestion. We first performed formal sex-by-age interaction tests in the three existing main-text age-GAM families, rather than introducing new outcomes. For each outcome, we compared the original additive model, Measure ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD, with a sex-specific age-trajectory model, Measure ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD. Nested-model interaction tests were conducted using ML fits, whereas the displayed trajectories were estimated with REML, consistent with the primary analyses.

After BH correction within each original analysis family, sex-by-age interactions were detected only for three Figure2 gradient-distribution features:lLG explained variance (q = 0.00272), cIG range (q = 0.0449), and cIG standard deviation (q = 0.0449). No interaction survived correction among the six Figure 3 hippocampus–cortical-hierarchy measures or the three Figure 4 geometry–function coupling measures.

In the sex-specific trajectories, the clearest difference concerned lLG explained variance: females showed a lower childhood level followed by a steeper increase and higher adolescent values, whereas males exhibited a more gradual increase. For cIG range and standard deviation, both sexes showed broadly similar inverted-U-shaped trajectories; the male trajectory was modestly higher through mid-to-late adolescence, with substantial overlap of the confidence intervals. The original combined-sex trajectory lay between, or closely followed, the two sex-specific curves. Thus, the principal developmental patterns are broadly consistent across sexes, while sex-related shifts are limited to a small subset of gradient-distribution features.

Revised manuscript text (Page 10):

“We additionally tested sex-by-age interactions across the previously reported developmental models. After FDR correction, significant interactions were identified for lLG explained variance and the range and standard deviation of cIG, whereas no sex-by-age interaction survived correction for the remaining primary developmental outcomes. Sex-disaggregated trajectories for these significant interactions are shown in Supplementary Fig. 4.”

(6) There have been reports of some distortions in inferior temporal regions after non-linear alignment to standard space in the HCP processing, which may affect hippocampal data sampling. Did the authors verify registration accuracy and absence of such distortions in their samples?

We thank the reviewer for raising this important concern regarding potential registration-related distortion. We clarified the registration and sampling chain and now explicitly distinguish native-space signal sampling from the subsequent use of a common coordinate system for group-level correspondence.

Crucially, the hippocampal fMRI time series were sampled in each participant’s native space: BOLD data were mapped back to the native anatomical space and sampled within the participant-specific hippocampal grey-matter ribbon onto the native HippUnfold mid-thickness surface. Likewise, hippocampal T1w/T2w measurements were sampled from the participant-specific native hippocampal surfaces. Thus, neither the fMRI nor the T1w/T2w hippocampal measurements was obtained by sampling voxels after nonlinear transformation into a standard medial-temporal-lobe space. This design avoids standard-space deformation influencing the extraction of these hippocampal signals and intensity measures. The subsequent common surface coordinate is used to establish vertex correspondence across participants for group-level analyses, rather than to define the native-space signal samples themselves.

We also performed visual quality control of the HippUnfold registration and surface reconstruction, inspecting the alignment of each participant’s hippocampal segmentation and reconstructed surfaces with the native T1-weighted anatomy. The documented mask-overlap quality-control procedure further showed Dice coefficients above 0.7. The paired inner and outer surfaces define the mid-thickness sheet used for ribbon-constrained sampling, which is particularly suitable for the variable folding geometry of the hippocampus.

(7) Can the authors clarify how gene expression was analyzed for the hippocampus? Were HippUnfold models run across all donors separately, and probes were then sampled and co-registered? How did the authors handle data sparsity?

We thank the reviewer for this request for clarification. The full hippocampal transcriptomic workflow is described in the Methods subsection “Transcriptomic association analysis of the hippocampal gradients”. We clarify the procedure here to make the correspondence between the Allen Human Brain Atlas (AHBA) samples and the hippocampal gradients explicit.

We used AHBA microarray data from six donors. Donor-specific age- and sex-related effects were regressed from each probe before the normalized residual expression values were combined. We selected samples annotated as CA1, CA2, CA3, CA4, subiculum, or dentate gyrus from both hemispheres, yielding 188 hippocampal samples. The participant-specific native HippUnfold mid-thickness surfaces were transformed to MNI space and averaged to generate the group template mid-thickness surfaces. Each AHBA hippocampal sample was then matched to its nearest vertex on this template. Fifteen samples located more than 6 mm from the template surface were excluded, leaving 173 samples from six donors. The group-averaged hippocampal gradient value at the matched template vertex was assigned to each retained tissue sample.

We then used LASSO-PCR to model each gradient from the 173 × 58,692 normalized expression matrix. Principal-component analysis was first used to represent the correlated probe-expression structure, and LASSO regression was fitted on the retained component scores. The penalty parameter was selected by nested five-fold cross-validation, and generalizability was evaluated using ten repeated ten-fold cross-validation. Probe weights were subsequently reconstructed from the fitted component weights for the feature-deconstruction and enrichment analyses.

Thus, the transcriptomic analyses are group-template spatial associations between adult post-mortem AHBA samples and the group-averaged hippocampal gradients. They are not donor-specific developmental measurements, nor do they establish a causal molecular mechanism. We have retained the complete methodological description in the Methods subsection cited above and clarify the workflow here for ease of reference.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors aim to assess how the functional organisation of the hippocampus is related to the geometry and neurobiological differences of the hippocampus. In particular, the authors focus on the first three eigenvectors of hippocampal-cortical functional connectivity, based on non-linear dimensionality reduction on resting-state functional MRI data. Furthermore, the work aims to describe changes in these functional axes and their relation to other factors throughout youth and evaluate whether they are predictive of individual variations in cognition.

Strengths:

A major strength of this study is the attempt to replicate key findings across multiple developmental cohorts.

Weaknesses:

The major weaknesses of the manuscript center on gaps in technical transparency and several conceptual inaccuracies. The machine learning methodology used for cognitive prediction is scarce, leaving little means to evaluate whether the behavioral results suffer from data leakage or overfitting. The introduction sets up an oversimplified historical premise regarding the field's understanding and appreciation of hippocampal connectivity, and contains several incorrect references that throw doubt on the argumentation. Additionally, T1w/T2w signal intensity is incorrectly used as synonymous with myelin, despite gold-standard histological validation showing a non-significant correlation between T1w/T2w and myelin staining (Sandrone et al., 2013).

Appraisal of Aims and Conclusions:

The authors partially achieve their aims by illustrating certain age-related changes in hippocampal function; however, the correlative study design is not equipped to examine how these changes are "shaped" by geometry, myelination, or gene expression (especially the latter two). Furthermore, conclusions were often overstated based on small effect sizes.

Context and Field Impact:

This work adds to a growing body of literature focused on gradient-based representations of hippocampal topology. By applying these methods across a wide developmental age bracket, it provides a useful reference point for how the hippocampus and wider cortex interact during maturation. To improve utility to the neuroimaging and cognitive neuroscience communities, the nesting of subfields within the eigenvector topology should be addressed, too.

We thank Reviewer #2 for the careful assessment and for recognizing the value of replicating key findings across multiple developmental cohorts. We have addressed the specific concerns regarding cognitive prediction, historical framing, biological interpretation, effect-size interpretation, citation placement, and T1w/T2w signal in the detailed responses below. These revisions expand the prediction methods, clarify the interpretation of hippocampal gradients and subfields, recalibrate the developmental claims, and improve the precision of the supporting citations.

We also thank the reviewer for raising the need for a more precise interpretation of T1w/T2w signal. We agree that T1w/T2w intensity should not be used synonymously with myelin, and we have revised the manuscript throughout to refer to it as a myelin-sensitive but non-specific MRI contrast that may reflect multiple tissue properties. We respectfully clarify the interpretation of the cited Sandrone et al. study. We believe that the intended reference is Sandrone et al. (2023)[4], rather than 2013. This study tested the correspondence between T1w/T2w and Luxol Fast Blue staining specifically in corpus-callosum white matter; it did not include cortical gray matter or hippocampal tissue. Its callosal analysis did not show the expected positive correspondence between T1w/T2w and histological myelin staining (indeed, it reported a significant inverse correlation), but this result cannot establish the validity or invalidity of T1w/T2w as an index of myelin-sensitive microstructural variation in hippocampal gray matter. The authors also distinguished this white-matter result from prior evidence of cortical co-localization between high T1w/T2w signal and myelin-rich regions.

Accordingly, we do not interpret our hippocampal T1w/T2w findings as direct measurements of myelin content or cellular myelination. Rather, they indicate associations with an indirect MRI contrast that is sensitive to myelin-related, as well as other, tissue properties. We have revised the relevant Introduction, Results, Discussion, figure text, and Methods language to reflect this distinction.

We thank the reviewer for highlighting the importance of considering how hippocampal subfields are nested within the connectivity-eigenvector topology. This question has been addressed in our related subfield-specific study using the same HCP-D cohort and HippUnfold surface framework. We explicitly examined the distribution of the two long-axis gradients across the cytoarchitectonic subfields (Sub, CA1, CA2/3, and CA4–DG), their distinct cortical-connectome organization, and their associations with episodic memory (Zeng et al., 2025[5]). We have added a citation to this work to provide the relevant subfield-level context. The present study focuses on the continuous whole-surface organization and developmental trajectories of the three hippocampal functional gradients.

Revised manuscript text (Page 29):

“Continuous hippocampal gradients and cytoarchitectonic subfields

The continuous whole-surface topology examined here should not be viewed as separate from hippocampal cytoarchitectonic subfield architecture. Rather, it characterizes hippocampal-cortical connectivity organization across the unfolded hippocampal surface, including variation that extends across subfield boundaries. The proximal-distal association of cIG provides one link between this continuous topology and the Sub-CA-DG axis. Complementing the present whole-surface analysis, our recent subfield-specific study of the same HCP-D cohort examined how the two long-axis gradients are distributed across Sub, CA1, CA2/3, and CA4-DG. It further showed that their subfield-specific cortical-connectome organization was associated with episodic memory[5]. Taken together, these findings indicate that hippocampal functional gradients provide a unifying framework that relates continuous topology and cytoarchitectonic architecture to hippocampal-cortical network organization, developmental reconfiguration, and cognition.”

Reviewer #2 (Recommendations for the Authors):

(Methodological and Statistical Revisions)

(1) Prediction of Cognitive Performance:

Provide a comprehensive, step-by-step description of the machine learning pipeline used for cognitive prediction. Explicitly specify the features extracted, the exact estimator employed, the cross-validation strategy, and the precise measures taken to prevent data leakage.

We thank the reviewer for requesting clarification of the cognitive prediction analysis. We have added a dedicated Methods subsection describing the prediction framework and its safeguards against data leakage. We used hippocampal–cortical projection features to estimate episodic memory, cognitive flexibility, working memory, and inhibitory control, while including age, sex, scanning site, and mean framewise displacement as linear covariates.

To address the high dimensionality and correlation structure of the projection features, we used a PCA–LASSO framework. PCA generated component scores from the hippocampal–cortical projection features, and LASSO regression was fitted to these scores. The LASSO regularization parameter was selected using nested five-fold cross-validation.

Predictive performance was evaluated with age-balanced 10-fold cross-validation, using rounded age solely to stratify the outer folds. To prevent information leakage, all data-adaptive steps were completed using only the outer training data. These steps included feature transformations, estimation of linear covariate effects, PCA, and LASSO penalty selection. The fitted processing steps and model were then applied to the held-out fold. Performance was quantified by the squared Pearson correlation between cross-validated predicted and observed cognitive scores. We applied FDR correction across the 12 resulting gradient–cognition tests.

Revised manuscript text (Page 37-38):

“Cognitive prediction analyses

We used hippocampal–cortical projection features to predict episodic memory, cognitive flexibility, working memory, and inhibitory control. Age, sex, scanning site, and mean framewise displacement were included as linear covariates.

The model used a PCA–LASSO framework to address the high dimensionality and correlation structure of the projection-feature matrix. Principal-component analysis generated component scores from the hippocampal–cortical projection features. LASSO regression was then fitted to these scores.

Predictive performance was evaluated using age-balanced 10-fold cross-validation. Rounded age was used solely as the stratification label for the outer folds. Within each outer training fold, feature transformations, principal-component estimation, linear covariate effects, and LASSO penalty selection were fitted using training data only. These fitted transformations and model parameters were then applied to the held-out fold. Thus, held-out participants did not contribute to feature preprocessing, covariate estimation, component construction, or model tuning.

The LASSO regularization parameter was selected using nested five-fold cross-validation within each outer training set. Predictive performance was quantified as the squared Pearson correlation between cross-validated predicted and observed cognitive scores. We tested 12 gradient–cognition pairs from three hippocampal gradients and four cognitive measures. False-discovery-rate correction was applied across all resulting p-values.”

(2) Integration of Core Statistics:

Move the relevant test statistics, degrees of freedom, and FDR-corrected p-values for primary developmental claims from the Extended Data figures into the main text body to ensure transparency.

We thank the reviewer for emphasizing the need to make the statistical evidence underlying the extended developmental displays directly traceable. We have now added quantitative reporting for the three gradient-distribution features displayed in Extended Data Fig. 4 but not in Figure 2e, f. Specifically, the revised Results text reports the FDR-corrected age-related changes in range, skewness, and kurtosis.

We also created Supplementary Data 1 for the parcel-wise developmental trajectories shown in Extended Data Fig. 5f. This table provides the GAM statistics for all 360 cortical parcels for each hippocampal gradient, including the age-smooth F statistic, Δ adjusted R², raw and FDR-adjusted p values, and Yeo seven-network assignment. We added an explicit reference to this table immediately after the Extended Data Fig. 5f citation in the Results. These changes enable readers to inspect the numerical evidence underlying the Extended Data displays without inferring statistics from the figures alone.

Revised manuscript text

(Page 10):

“Beyond these features shown above, the ranges of lLG and qLG changed with age (lLG: ΔAdj. R² = 0.0098, p = 0.0017; qLG: ΔAdj. R² = 0.0044, q = 0.0148). lLG skewness and lLG / qLG kurtosis also changed with age, whereas qLG skewness and all three cIG measures did not survive FDR correction across the six distributional features of each gradient (Extended Data Fig. 4).”

(Page 15):

“Complete parcel-wise GAM statistics are provided in Supplementary Data 1.”

(3) Signal-to-Noise Ratio (SNR) Justification:

Provide an analytical justification demonstrating why vertex-wise probing at a 483-vertex density within the hippocampus does not suffer from too severe spatial oversampling or low SNR problems.

We thank the reviewer for raising the important concern that a dense hippocampal surface representation could create spatial oversampling or unstable vertex-level measurements. We have now added a quantitative assessment of the native HippUnfold mesh spacing. The 483-vertex representation is the den-2mm HippUnfold template, comprising 419 hippocampal and 64 dentate vertices per hemisphere. We measured distances between adjacent vertices on all 2,608 un-smoothed native T1w mid-thickness surfaces from the 652 HCP-D participants. Across 1,765,616 unique mesh edges, the pooled median distance was 2.01 mm (IQR, 1.43–2.57 mm), and 78.3% of edges were between 1 and 3 mm. Thus, the native mesh is centered on the 2-mm spatial scale of the BOLD acquisition rather than constituting a submillimeter sampling grid. The remaining local variability reflects individual anatomy and the triangular surface geometry. These results are shown in Supplementary Fig. 7.

We noted that BOLD data were sampled in each participant’s native anatomical space using partial-volume-weighted ribbon-constrained mapping between the paired inner and outer hippocampal surfaces. Each vertex value is therefore a weighted estimate from voxels within the hippocampal grey-matter ribbon, rather than a nearest-voxel sample. Importantly, the 483 vertices were not treated as independent fMRI observations. Spatial dependence among neighboring vertices is expected, whereas the developmental inference was performed on participant-level gradient-derived features and cortical-projection measures, with sex, site, hemisphere, and mean framewise displacement included as covariates. Replication of the principal organizational patterns in the independent NKI-RS and CBD samples provides additional evidence that the reported gradient findings are unlikely to be materially driven by low-SNR or spatial-oversampling artefacts.

Revised manuscript text (Page 35): “The vertex spacing was set at approximately 2 mm, close to the 2.0 mm isotropic fMRI voxel size. The distribution of distances between adjacent vertices across all native-space mid-thickness surfaces was centered near this target spacing (median, 2.01 mm; interquartile range, 1.43–2.57 mm; 78.27% of edges, 1–3 mm; Supplementary Fig. 7).”

(4) Justification for Eigenvector Exclusion:

Strengthen and clarify the rationale for excluding eigenvectors 4 and 5 from subsequent analyses, particularly since they appear above the "knee" of the variance explained plot.

We thank the reviewer for pointing out that the variance-explained profile and the decision about biological interpretability are distinct considerations. We have clarified that G4 and G5 were excluded from the primary interpretation because their biological meaning and spatial interpretation were not sufficiently clear, not because their variance contribution was negligible. We have added this distinction to the Results.

Revised manuscript text (Page 9): “We did not include G4 and G5 in the current interpretation because their biological significance was not sufficiently clear; this decision reflected interpretability rather than negligible explained variance.”

(Interpretation)

(1) Eigenvector Interpretation and Topography:

Delineating how continuous gradients relate to or interact with discrete histological subfields would provide a more biologically grounded interpretation than relying strictly on geometry. Naming the eigenvectors based on weak geometric associations (especially in the case of G3) risks obfuscating the complex variation within the data. For full transparency, all linear and quadratic associations with all anatomical axes should be systematically reported, and a more descriptive or neutral nomenclature should be considered.

We thank the reviewer for this important comment. We agree that the biological interpretation of continuous hippocampal gradients should not be framed as geometry in isolation. We have therefore clarified that the posterior–anterior and proximal–distal coordinates are complementary anatomical descriptions of hippocampal biological organization, rather than biologically empty geometric axes.

In particular, the posterior–anterior axis captures the hippocampal long-axis organization, whereas the proximal–distal axis follows the iso-to-allocortical topology from subiculum through the Cornu Ammonis fields to dentate gyrus. This latter direction is topologically aligned with the discrete hippocampal subfields, which are themselves defined by differences in cytoarchitecture. Thus, the geometric coordinate system and the cytoarchitectonic organization provide two complementary descriptions of the same underlying hippocampal topology, rather than mutually exclusive interpretations. We revised the text to make this relationship explicit and to avoid implying that the observed gradients provide a direct histological measurement.

We also clarify that the reported gradient–axis relationships were not selected post hoc from a single geometric comparison. We systematically evaluated linear and quadratic associations between each of the three functional gradients and both intrinsic anatomical axes, and additionally assessed higher-order relationships where warranted. Figure 2b–d shows the strongest statistically supported relationship for each gradient: a linear posterior–anterior association for G1, a quadratic posterior–anterior association for G2, and a cubic proximal–distal association for G3. The remaining axis associations are reported in Extended Data Fig. 2. Accordingly, the descriptive names are based on comparative assessment of the full set of candidate geometric models, while G1–G3 remain the primary neutral identifiers throughout the manuscript.

Revised manuscript text (Page 9): “This gradient follows the medial–lateral, iso-allocortical organization of the hippocampus and is topologically aligned with cytoarchitectonically differentiated subiculum, CA fields and dentate gyrus.”

(2) Balanced Nomenclature:

Elevating the cortical component to a higher-order conceptual term ("hierarchy") while leaving the hippocampal counterpart strictly geometric ("gradients"), given that both metrics are derived using equivalent non-linear dimensionality reduction.

We thank the reviewer for highlighting this asymmetry in terminology. We agree that applying the term “hierarchy” to the cortical component without defining its evidential basis could be confusing, particularly because both cortical and hippocampal maps are obtained using nonlinear dimensionality-reduction methods.

The term cortical functional hierarchy does not arise simply from estimating a cortical gradient. It originates from longstanding models of cortical organization in which sensory systems occupy relatively lower-order positions and progressively integrated association systems occupy higher-order positions. This framework has subsequently been formalized at the macroscale as the reproducible unimodal-to-transmodal axis of functional connectivity and has been supported by convergent evidence from cortical microstructure, structure-function coupling, connectivity architecture, and transcriptomic specialization[6-9]. We have clarified this historical and evidential basis in the revised manuscript.

In the present study, the cortical functional-hierarchy map is therefore used as an independently established reference map of continuous cortical organization, rather than as a new hierarchy inferred from our hippocampal data. We use this term operationally and non-causally: it indexes each cortical region’s position along the established unimodal-to-transmodal functional-connectivity axis.

Crucially, this terminology does not assign greater biological importance to the cortical measure. Hippocampal functional gradients are the primary object of the present study, and determining their structural and functional significance is a central aim. We therefore examine their associations with hippocampal anatomical coordinates and geometric modes, myelin-sensitive MRI, transcriptomic variation, cortical functional organization, and cognition. We retain the neutral labels lLG, qLG, cIG and “hippocampal functional gradients” because they describe empirically derived axes without presupposing a biological interpretation. As convergent anatomical, microstructural, functional, and comparative evidence accumulates, a more specific organizational terminology for particular hippocampal gradients may become justified. Thus, the present distinction between “cortical functional hierarchy” and “hippocampal functional gradients” reflects the evidential role of each measure in this study, rather than a difference in scientific importance or in the legitimacy of their structure-function interpretation.

Revised manuscript text (Page 14): “Here, FH denotes the established unimodal-to-transmodal ordering of macroscale cortical functional organization, rooted in longstanding models of hierarchical cortical processing and subsequently formalized using functional-connectivity gradients.”

(3) Refinement of Textual Tone and Claims:

• Remove causal verbs (e.g., "sculpts", "constrains") when describing correlations between functional gradients, structural metrics, and cognitive scores, replacing them with appropriate relational or correlational language.

We thank the Reviewer for reinforcing the need for this terminology correction. We agree that the request to remove causal verbs describes the same manuscript-wide claim-calibration issue addressed in our response to Reviewer #1, Recommendation 1. We have therefore applied the consolidated terminology revision across the overlapping sections, including the descriptions of functional gradients, structural measures, MRI intensity, and cognitive scores.

• Temper the interpretation of the ~5% variance explained in the maturation analyses, ensuring that this modest effect size is not framed as a massive macroscale reorganization or "decoupling."

We thank the reviewer for noting that the age-related variance explained by some global gradient features is modest. We agree that the reported ∆Adjusted R² values quantify age-related variation in a specific descriptive summary—for example, the explained variance or standard deviation of a gradient, or a summary measure of geometry–function coupling—after accounting for the covariates in the model. They should therefore not be interpreted as the proportion of the entire hippocampal functional-connectivity organization that changes with age, nor as a standalone measure of the magnitude of hippocampal reorganization.

Our interpretation of developmental reorganization does not rely on these global summary statistics alone. The spatially resolved hippocampal–cortical connectivity organization shows complex variation across the hippocampal surface (Extended Data Fig. 3). In addition, the age-related analyses of hippocampal gradient projections identify distributed and system-specific developmental changes across the cortex (Figure3e–g; Extended Data Fig. 5f). Together, these complementary analyses support the interpretation that hippocampal–cortical functional organization undergoes a distributed developmental reorganization. We thus retained the description of a distributed developmental reorganization of hippocampal–cortical functional organization, while clarifying that this conclusion is supported by the spatially resolved analyses rather than by the magnitude of any individual global-summary effect size.

Revised manuscript text (Page 15): “This distributed developmental reorganization of hippocampal–cortical functional organization, which correlates with increasingly complex hierarchical cortical processing, may link to the maturation of episodic memory and executive function (EF)—a set of top-down mental processes potentially associated with cortical hierarchical organization.”

Correction of Inaccuracies

(1) Historical Context:

Revise the introduction to accurately reflect that distributed network connectivity has long been recognized as central to hippocampal function and memory, rather than framing it as a highly novel realization.

We appreciate the opportunity to clarify the historical framing. The manuscript did not intend to present distributed hippocampal-cortical connectivity as a newly discovered concept; its intended contribution is a developmental, topographic analysis of hippocampal functional gradients. We revised the surrounding wording to make this distinction explicit while retaining the established literature on distributed hippocampal connectivity.

Revised manuscript text (Page 4): “Distributed hippocampal-cortical connectivity has long been central to models of memory and cognition[10-15].”

(2) Citation Accuracy:

Address several inaccuracies where cited literature does not support the accompanying claims. I would like to highlight that this is one of the most concerning aspects of the paper, as it suggests that (at best) the primary authors made several mistakes in their citations that went unnoticed by co-authors, or (worse) it could appear as if the authors have not read the papers they cited, despite them being key to the field.

We thank the reviewer for emphasizing the importance of citation accuracy and take this concern seriously. We re-checked the source papers and the placement of the citations underlying the three statements raised below. We identified one genuine citation-placement error introduced during iterative revision: Shohamy and Turk-Browne (2013) was inadvertently retained with a developmental statement after being moved from the preceding statement on the hippocampus’s broad cognitive involvement. We have corrected this placement.

The other two cases were not instances of uncited or unread literature, but the cited papers did not support the precise wording used in the manuscript. Strange et al. was relevant to longitudinal-axis functional organization but not to the proximal–distal cytoarchitectonic context, and Vos de Wael et al. identified medial–lateral variation within separately analyzed subfields but did not establish a whole-hippocampus myelin gradient. We have therefore removed or replaced these citations, revised the associated claims, and now use Genon et al. (2021)[16] for the appropriate anatomical and microstructural-organizational context. These revisions distinguish direct evidence, anatomical interpretation, and indirect MRI-based microstructural measures more clearly.

a) "It was traditionally assumed that the hippocampus undergoes its most significant development in infancy and early childhood and achieves full maturity by the end of this period13" - Shohamy et al. do not discuss hippocampal development.

We thank the reviewer for identifying this citation mismatch. We agree that Shohamy and Turk-Browne (2013) does not support a claim about hippocampal developmental timing. During iterative manuscript revision, this reference was inadvertently retained with the developmental statement after being moved from the preceding sentence concerning the hippocampus’s broad involvement in cognition. We have restored it to that preceding sentence.

The revised historical statement is now supported by and Ghetti and Bunge (2012)[17] and Bauer (2007)[18], which describe earlier accounts emphasizing hippocampal development in infancy and early childhood. We further clarify immediately thereafter that more recent evidence supports continuing, regionally differentiated hippocampal development beyond early childhood.

Revised manuscript text (insert on Page 4): “Earlier accounts proposed that hippocampal development was most consequential in infancy and early childhood[17-18].”

b) "This gradient exhibits similarities to the previously established cytoarchitectonic variations within the hippocampus4,27. We hence termed it the cubic iso-allocortical gradient (𝑐𝐼𝐺)." - Strange et al., does not mention cytoarchitecture, and Genon et al., is only a secondary source on the matter.

We thank the reviewer for this important citation correction. We agree that Strange et al. primarily concerns functional specialization along the hippocampal longitudinal axis and does not provide appropriate support for a claim regarding the proximal–distal or medial–lateral cytoarchitectonic organization. We have therefore removed this citation from the relevant sentence.

We retained Genon et al.[16] because this review systematically synthesizes the major dimensions of human hippocampal organization and identifies the medial–lateral dimension as a key organizational axis associated with cytoarchitectonic differentiation. In our data, cIG showed a significant cubic association with the proximal–distal coordinate (Figure 2b). This coordinate is topologically aligned with the medial–lateral, iso-allocortical organization spanning subiculum, CA fields and dentate gyrus. We have clarified that Genon et al. is cited to provide this anatomical-organizational context, rather than as direct histological validation that the fMRI-derived cIG measures cytoarchitecture.

Revised manuscript text (insert on Page 9): “This gradient follows the medial–lateral, iso-allocortical organization of the hippocampus and is topologically aligned with cytoarchitectonically differentiated subiculum, CA fields and dentate gyrus[16].”

c) "Moving to the mesoscopic scale, myelin content has been found to exhibit a significant medial-lateral gradient along the hippocampus26." - this is not evidenced by the referenced paper (Vos de Wael et al.), and it is not true (see Abrahim et al., 2010).

We thank the reviewer for raising this important distinction. We agree that Vos de Wael et al. does not support a claim of a continuous medial–lateral gradient in hippocampal myelin content. Although that study identified medial–lateral variation in functional-connectivity organization when hippocampal subfields were examined separately, it was not designed to establish a whole-hippocampus myelin gradient. We have therefore removed Vos de Wael et al. as support for this statement and revised the text to remove the unsupported myelin interpretation.

We now cite Genon et al. (2021), which synthesizes evidence that local hippocampal microstructural variation, including T1w/T2w-intensities-based estimates that are sensitive to myelin, is organized predominantly along the medial–lateral and ventrodorsal axes. The review further notes partial spatial overlap between medial–lateral functional gradients, myelin-sensitive MRI estimates, and subfield differentiation.

We respectfully note that Ábrahám et al. (2010) does not contradict this spatial interpretation. Its histological study examined the developmental timing and layer-specific distribution of myelination across ages; it did not test a surface-wide medial–lateral spatial pattern across the hippocampal formation. It is therefore not evidence for a continuous medial–lateral myelin gradient, but neither does it provide evidence against such an organizational pattern.

Revised manuscript text (insert on Page 5): “local microstructural variation in the hippocampal formation, including myelin-sensitive T1w/T2w intensities, is organized predominantly along the medial–lateral and ventrodorsal axes along the hippocampus and partially overlaps with subfield differentiation[16].”

(3) Other:

a) Clearly define or rephrase ambiguous phrasing, such as "Myelination during nurturing process."

We thank the reviewer for identifying this ambiguous wording. We agree that “nurturing process” was imprecise in this general background statement. We have therefore revised the Introduction to state: “Myelination during brain development has been identified as a key factor in neural plasticity and circuit refinement, affecting neural activity synchronization[19-23].”

b) Re-evaluate the evolutionary claim in the discussion. It's unclear why the authors assert that the longitudinal axis is uniquely more conserved. The iso-to-allocortical axis is highly conserved, observed even in reptiles.

We thank the reviewer for this important clarification. We agree that the original Discussion conflated the evolutionary conservation of hippocampal anatomical axes with the interpretation of the functional gradients. We have therefore removed the statements that the linear long-axis gradient is more evolutionarily conserved and may consequently depend more on shared gene-expression patterns, as well as the statement that cIG reflects the portion of the hippocampal–cortical connectome influenced by cytoarchitectonic differentiation.

We retained the broader comparative interpretation, but revised it to make its evidential status explicit. G2 showed the strongest association with cortical functional hierarchy. Given the greater prominence of hierarchical cortical processing in humans and macaques than in marmosets or rodents, this association raises the possibility that G2 is less evolutionarily conserved than G1 and G3. However, this is a hypothesis motivated by the observed cortical association, rather than a conclusion directly tested by the present human developmental data. We now state this limitation explicitly and identify direct cross-species comparisons as necessary to evaluate it.

Revised manuscript text (insert on Page 25): “Given the greater dominance of hierarchical processing in humans[24] and macaques[25] in contrast to other species such as marmosets[26] or rodents[27], the strong association of quadratic long-axis gradient with cortical functional hierarchy raises the possibility that it is less evolutionarily conserved than linear long-axis gradient and cubic iso-allocortical gradient. Future cross-species comparisons could test this hypothesis.”

c) Frame the T1w/T2w intensity variations cautiously as an indirect proxy reflecting multiple tissue properties, incorporating recent literature (e.g., Sandrone et al., 2023) to explicitly acknowledge the confounding effects (e.g., transmit field bias).

We thank the reviewer for emphasizing the need for a cautious interpretation of T1w/T2w intensity. We agree that it should not be treated as synonymous with myelin or as a direct measure of myelin content. Following its established use as a myelin-sensitive cortical MRI contrast (Glasser and Van Essen, 2011), we now consistently describe T1w/T2w as myelin-sensitive measures. Its variation may reflect myelin-related tissue properties, as well as other tissue and acquisition factors, including transmit-field bias.

We have incorporated Sandrone et al. (2023)[4] as an important qualification. We respectfully note that this study evaluated corpus-callosum white matter and did not examine cortical gray matter or hippocampal tissue. It therefore supports caution in interpreting T1w/T2w, but cannot itself establish or invalidate the hippocampal gray-matter association reported here. Accordingly, we interpret our result only as an association between hippocampal functional gradients and an indirect MRI contrast, not as evidence of myelin, cellular myelination, or a myelin-mediated developmental mechanism. We revised the relevant Introduction, Results, Figure 5 legend, Discussion, and Limitations accordingly.

Revised manuscript text (insert on Page 30): “T1w/T2w intensity was treated as an indirect, myelin-sensitive MRI proxy influenced by multiple tissue and acquisition factors, not as direct histological myelin content.”

Reference

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Author response:

We thank the Editors and reviewers for their close reading of our work and valuable comments. We appreciate their recognition of the foundational nature of our study. The reviews suggest multiple improvements that we plan to implement in a revised version, including the following: validation of appearance labels; short self-contained example code for analysing the dataset; greater comparison with prior work in the discussion; more details in the methods. The reviews also make many suggestions for improving the presentation, wording, and clarity of the work. In particular, we acknowledge that we used incorrect terminology in referring to the axes rather than the semi-axes of fitted ellipsoids. The revision will correct this error and provide the full parameters of the ellipsoid fits (r0, r1, r2) in the supplementary data, allowing the consistency of these fits with mitochondrial volume to be appreciated. We did identify that the values of one of the mitochondrial variables not used for the analysis in the paper (r2) had been corrupted in the uploading of the publicly available hemibrain:v1.2.1 dataset to neuprint. Accordingly, we have generated hemibrain:v1.2.3 which restores the original, correct and uncorrupted values of this variable.

Author response:

We thank the reviewers and the Reviewing Editor for their careful and constructive assessments. We find the reviews fair and helpful, and we plan to revise the manuscript along the lines they suggest. In brief:

Scope of the conclusions (Reviewer #1):

We can see how a reader may get the impression that some of our conclusions go beyond what the experiments directly establish. In the revision we will:

- Describe the genetic tools as targeting neuronal populations (DAN clusters) rather than identified single neurons, and adjust statements about neuronal identity accordingly.

- Rephrase the description of the time-course results, to emphasize that the shift from aversive to appetitive only appears across experiments and that some single experiments may only show a shift to neutrality. This should help moderate claims about positive valence.

- State explicitly that our non-contingent comparison used continuous pre-exposure rather than a yoked control. It therefore shows that simple non-contingent exposure is insufficient but does not isolate agency as the causal variable.

- Better motivate the design changes between the original screen and follow-up joystick experiments.

- Frame the “common currency” hypothesis more cautiously throughout.

Clarity and accessibility (Reviewer #2):

We appreciate that the manuscript is hard to follow for readers outside the field. We will revise the final sentence of the Abstract and clarify what we mean by a dopaminergic “reporter for a specific goal”. We will also spell out how the contrast between a tethered fly and a free-flying fly in a maze bears on this, and what we mean by “control” versus “lack of control” of the environment. In the Introduction and Discussion we will make clearer which cited studies propose or favor the “common currency” view, including Jovanoski and Waddell (2025), and which ones merely bear on it.

Conceptual framework (Reviewer #3):

We will make our assumptions linking the role of DANs in classical conditioning to their expected effects in operant paradigms more explicit. The reference to the Heisenberg and Wolf (1991) scheme as a suitable level of explanation was particularly helpful and we will thrive to develop our hypotheses at the same level. At least for the designers of the original screen (BB and CR), the lack of consistent effects was clearly unexpected, or we would have designed the experiments differently. We will justify these expectations and from this why we consider this negative result to be so informative.

Code availability (Reviewing Editor): We will deposit the code in a repository with a permanent DOI, such as Zenodo, in addition to GitHub.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Olmstead et al. present a single-cell nuclear sequencing dataset that interrogates how hippocampal gene expression changes in response to distinct physiological stimuli and across circadian time. The authors perform single-nucleus RNA sequencing on mouse hippocampal tissue after (1) kainic acid-induced seizure, (2) exposure to an enriched environment, and (3) at multiple circadian phases.

The dataset is rigorously collected, and a major strength is the use of the previously established ABC taxonomy from Yao et al. (2023) to define cell types. The authors further show that this taxonomy is largely independent of activity-driven transcriptional programs. Using these annotations, they examine activity-regulated gene expression across neuronal and glial subclasses. They identify ZT12, corresponding to the transition from the light to the dark period, as transcriptionally distinct from other circadian time points, and show that this pattern is conserved across many cell types. Finally, they test how circadian phase influences activity-dependent gene expression by exposing mice to an enriched environment at different times of day, and report no significant interaction between circadian phase and enriched environment exposure.

A crucial consideration for users of this dataset is the potential confounding effect between circadian phase and locomotor activity. This is particularly relevant because dentate gyrus activity is strongly modulated by locomotion. The authors acknowledge this issue in the Discussion and provide useful guidance for how to interpret their findings, considering this confound.

We thank the reviewer for their accurate and thoughtful summary of the ACT-DEPP dataset and the key experimental design and analytical choices that form the basis of the study. We agree that circadian phase and locomotor activity are major confounders that are irreconcilable in the current study. We have modified our Discussion of this point to consider future studies which would be able to delineate the two (lines 403-406)

Taken together, this dataset represents a useful resource for the neuroscience community, particularly for investigators interested in how novel experience and circadian phase shape activity-related and immediate early gene expression in the hippocampus

Reviewer #2 (Public review):

This manuscript presents the ACT-DEPP dataset, a comprehensive single-nucleus RNA-sequencing atlas of the mouse hippocampus that examines how activity-dependent and circadian transcriptional programs intersect. The dataset spans multiple experimental conditions and circadian time points, clarifying how cell-type identity relates to transcriptional state. In particular, the authors compare stimulus-evoked activity programs (environmental enrichment and kainite-induced seizures) with circadian phase-dependent transcriptional oscillations. They also identify a transcriptional inflection point near ZT12 and argue that immediate early gene (IEG) induction is broadly maintained across circadian phases, with minimal ZT-dependent modulation.

Strengths:

The study is ambitious in scope and data volume, and outlines the data-processing and atlasregistration workflows. The side-by-side treatment of stimulus paradigms and ZT sampling provides a coherent framework for parsing state (activity) from phase (circadian) across diverse neuronal and non-neuronal classes. Several findings - especially the ZT12 "inflection" and the differential sensitivity of pathways across subclasses - are intriguing.

Weaknesses:

(1) The authors acknowledge, but do not adequately address, the fundamental confounding factor between circadian phase and spontaneous locomotor activity. The assertion that these represent "orthogonal regulatory axes," based on largely non-overlapping DEGs, may be overstated. The absence of behavioral monitoring during baseline is a major limitation.

We agree that circadian phase and locomotor activity are irreconcilable confounders in the current study. We have removed the phrase “orthogonal regulatory logic.” This point is disclaimed as the leading point in our Limitations section. We expand on this section to consider future studies which would be able to delineate the two (lines 403-406).

(2) The statement "Thus, novel experiences and seizures trigger categorically distinct transcriptional responses-with respect to both magnitude and specific genes-in these hippocampal sub regions" is overstated, given the data presented. Figure 2A-B shows that approximately one-third of EE-induced DEGs at 30 minutes overlap with KA DEGs, and this overlap increases substantially at 6 hours in CA1 (where EE and KA responses become "fully shared"). This suggests the responses are quantitatively different rather than "categorically distinct."

We have modified the sentence (lines 127-129) to state: “Thus, novel experience and seizure induce transcriptional programs that differ greatly in magnitude and, apart from CA1 after 6 hours, contain stimulus-specific genes.” We have additionally modified the section title to de-emphasize stimulus-specificity.

(3) In Figure 4B, "active cells" are defined as those with >=3 of 15 IEGs above the 90th percentile, with thresholds apparently calibrated in CA1. Because baseline expression distributions differ across subclasses, this rule can bias activation rates across cell types.

The baseline expression thresholds were computed for each CA1 Supertype, e.g. CA1 69-1, 702, etc. (Figure 4D).

(4) Few genes show significant ZT × stimulus (EE or seizure) interactions, concentrated in neuronal populations. Given unequal nucleus counts and biological replicates across subclasses, small effects may be underpowered.

We agree with the observation that our measurements may be underpowered to observe small effects. The nuances of our DGE methodology are discussed below under Reviewer 2’s Recommendation #3.

(5) In Figure 6 I, J, the relationship between the highlighted pathways/functions and circadian phase is not yet explicit.

We agree that there is no obvious relationship for ZT-based changes in expression among genes in shared sets highlighted in Figures 6I-J. However, their enrichment among the small set of 13 significantly interacting genes genome-wide merits remark as we have done so here. What functional implications these observations have is the subject of future experiments.

(6) Line 276-280: The enrichment of lncRNAs at ZT12 in CA1 is intriguing but underdeveloped. What are these lncRNAs, and what might they regulate?

Gene symbols were ascertained by mapping reads to the GRCm39-113 mouse genome in Parse Bioscience’s Trailmaker pipeline (Methods). GRCm39 returns gene biotype annotations, which is how we determined these genes were lncRNAs. A literature search for these gene symbols found that all 12 are predicted or uncharacterized loci without functional experimental data.

Overall, most descriptive conclusions are supported (e.g., broad phase-robustness of classical IEGs; an inflection near ZT12). Claims about the separability/orthogonality of activity vs circadian programs, and about categorical distinctions between EE and KA responses, would benefit from more conservative wording or additional analyses to rule out behavioral and power-related alternatives.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I have a few suggestions for additional analyses and clarifications that could further strengthen the study:

(1) KA responsive populations and spatial context

In Figure 2, the authors show that KA-responsive cells cluster within two supertypes, which may 99 represent seizure-specific populations. Could the authors leverage the spatial transcriptomic data 100 from Yao et al. to ask whether there is a specific cell type or subregion within the dentate gyrus 101 that is predisposed to express the seizure-associated gene programs identified in Figure 2?

We thank the reviewers for this interesting analysis suggestion. We have added Figure 2—figure supplement 6 as an exploration of the spatial distribution of DG Supertype 138-3. We find that these cells are predominantly located in dorsal hippocampus, although are sparsely distributed throughout all of hippocampus.

(2) Baseline circadian modulation of canonical IEGs

In the Discussion, the authors note that canonical immediate early genes do not overlap with circadian differentially expressed genes, citing results from Figure 5. However, the current 109 analyses do not directly show how canonical IEG expression varies across the circadian cycle at 110 baseline. It would be helpful to include a focused visualization, for example, a heatmap or line plot 111 of IEG expression across circadian time points, to more directly support this conclusion.

We have added Figure 6—figure supplements 1-2. These plots demonstrate low variation of IEG expression within the standard environment across ZTs. EE-induction is likewise similar across ZTs in CA1. DG demonstrates less consistent induction relationships, likely due to dramatically low abundances leading to noisy expression estimates.

(3) Neurogenesis-related signatures

Given that dentate gyrus cells are included in the dataset, it may be informative to comment on neurogenesis-related transcriptional programs. For example, can the authors report whether markers of adult-born granule cells or progenitor populations are detected, and whether genes associated with neurogenesis are modulated by experience (seizure or enriched environment) or circadian phase? Even a brief analysis or summary would likely be of interest to the community.

We do capture a small population of immature neuronal cells (IMNs) in our dataset that are likely the product of dentate neurogenesis (Figure 1B). Our experiment was not adequately designed to detect the origin of these cells, nor determine whether EE induces changes in rate of neurogenesis or cell fates. However, we can measure the effects of acute EE on the preexisting IMN population present at the time of experimentation. We have added Figure 2—figure supplement 7 to examine this topic. We observe that hours of EE exposure instead of minutes is necessary to induce transcriptional changes. Interestingly, many of the DEGs observed encode neurotransmitter receptor subunits or intercellular adhesion proteins.

Reviewer #2 (Recommendations for the authors):

Behavioral confounding factor: Please provide locomotor activity measures aligned to ZT for the relevant cohorts (e.g., wheel counts or video tracking), or at minimum, discuss how ZT-dependent changes in arousal/locomotion could contribute to the observed transcriptional differences and how your analyses mitigate this confounding factor. Including locomotion as a covariate in pseudobulk models or presenting matched restraint controls would be helpful.

We did not collect locomotion data on the mice and so are unable to include it as a covariate in any analyses. We place the Limitations subsection at the beginning of our Discussion and disclose the confounding effect of locomotion/arousal as a main limitation of this study. 

It is well established that mice increase locomotor activity in the hour preceding the dark phase (i.e. during ZT 11-12) [1]. Similarly, in vivo neurophysiological studies of hippocampus during locomotion consistently demonstrate that neuronal cells in hippocampus exhibit spatially tuned activity that increases as an animal navigates an environment compared to when it is stationary [2]. If locomotion were to exhibit major influence on gene expression in our experiment, it is reasonable to assume that we would observe such effects in IEGs. Nevertheless, we do not observe changes in baseline IEG expression across ZTs (Figure 6—figure supplement 1-2). Based on this albeit circumstantial evidence, we conclude that circadian influences on gene expression are likely to predominate over locomotor ones in the absence of other manipulations.

What may explain this lack of IEG induction across dramatically different locomotor phases? It is possible that locomotion-dependent effects on neuronal activity are insufficient to drive activity-dependent changes without instructive learning signals within the hippocampal circuit. One speculative mechanism for this could be that, in the standard environment (i.e. the animal’s home cage), the lack of strong plasticity events such as dendritic plateau potentials [3] fails to overcome the signaling threshold(s) necessary to induce activity-dependent transcriptional programs. It also remains possible that locomotion-induced transcriptional changes involving hundreds of genes such as that observed in Figure 5 are coordinated through processes independent of canonical IEG induction.

(2) "Active cell" definition: Please provide (i) a sensitivity analysis varying the percentile cutoff (e.g., 80/85/95%) and the number of IEGs required (2-4), and (ii) a complementary analysis using continuous activity scores (e.g., AUCell or ssGSEA) with concordance to the binary call reported (ROC/PR or agreement metrics). Subclass-specific thresholding or normalization would further mitigate bias; reporting the fraction of "active" cells per subclass under each parameter set would be helpful.

We have added Figure 4— figures supplements 1-2 to incorporate all these requested analyses. Rather than rely on an external library to construct an IEG module score, we employ a simple z-scoring index of the 15 IEGs used in Figure 4B, D, E to overcome the technical challenges unique to this set of low-abundance genes.

From these requested analyses, we find that ROC curves were extremely accurate at classifying active and inactive cells based on a continuous activity IEG score (AUC > 0.985, Figure 4 — figure supplement 2). Precision-recall curves were also constructed, which demonstrated decreased—although still robust—classification of cell activity state in SE. This is consistent with the performance of precision/recall tradeoff between conditions when there is an imbalance of active/inactive cells in the underlying populations (see Figure 4B). When investigating the decreased PR-accuracy in SE, we observed that discordant classifications were likely to arise when a single IEG was elevated enough to significantly increase the composite score, leading to a spurious classification as “active” with the continuous scoring method when it would not meet the 3-gene threshold in the other method.

Finally, we note that we already employed supertype-specific thresholding to set baseline thresholds for each CA1 sub-population.

(3) Interaction effects and power: Please (a) report per-subclass effective sample sizes and replicate numbers, (b) re-analyze with a complementary framework (limma-voom or edgeR) and, where possible, (c) include sample-level mixed-effects models (animal as a random effect; pseudobulk counts or cell-fraction outcomes). Presenting effect sizes with uncertainty (e.g., forest plots) would improve interpretability beyond binary FDR thresholds.

We have added Figure 2—figure supplements 1-5; and Figure 3—figure supplement 1 to address these requests and included a new paragraph in the Results section (lines 130-146) describing how these different methods perform comparatively on our dataset. We observe that these methods perform similarly under most conditions, but that DESeq2 shrinkage—the method used for all DGE analysis in the main figures—aggressively forces estimated fold-change toward zero in certain conditions with high variance. We maintain our original conclusion that Type I error rate is adequately minimized. However, Type II error rate in our DGE analyses may be higher with DESeq2 under certain conditions compared to other frameworks.

We modified our Discussion to expand on these findings (lines 415-424) and disclose to the reader that “Our findings should be interpreted as a conservative observation of activity- and circadian-dependent changes in gene expression.” We thank the reviewer for these suggestions which have significantly improved the analytic rigor of the project and revealed its potential technical shortcomings.

(4) Figure 6 I,J : Please make clear whether these pathways are simply enriched among DE genes or whether they exhibit bona fide circadian modulation.

The 13 significant genes ascertained through the interaction analysis presented in Figure 6I-J were manually annotated through literature review, given the feasibility from such a small number of DEGs. The pathways described—endocannabinoid synthesis, signaling and excitability, and chromatin remodeling/gene expression—were all cellular processes implicated by literature review of the gene list. From this, we conclude that these processes are influenced by an interaction between circadian- and activity-dependent induction of gene expression after controlling for their individual effects.

References

(1) Eckel-Mahan, K. L. et al. Circadian oscillation of hippocampal MAPK activity and cAMP: implications for memory persistence. Nat Neurosci 11, 1074–1082 (2008).

(2) Buzsáki, G. Theta Oscillations in the Hippocampus. Neuron 33, 325–340 (2002).

(3) Bittner, K. C., Milstein, A. D., Grienberger, C., Romani, S. & Magee, J. C. Behavioral time scale synaptic plasticity underlies CA1 place fields. Science 357, 1033–1036 (2017).

Author response:  

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Comments on revised version.

The authors have revised their manuscript to clarify that molecular analyses have not yet occurred and have resolved the technical/publication issues with the figures. I look forward to seeing these tools used in future publications to answer important questions in Blastocystis research.

We are grateful to Reviewer 1 for their careful and constructive assessment of our revised manuscript. We are pleased that the revisions have satisfactorily addressed their previous concerns, and we sincerely appreciate their recognition of the value of our work.

Reviewer #3 (Public review):

Comments on revised version.

The revised version provides sufficient clarity and appropriate visual presentation. Some confusion evidently arose due to my misunderstanding, so I thank the authors for their comprehensive clarifications and patience.

We are grateful to Reviewer 3 for their careful reading of the revised manuscript and for the additional constructive suggestions. We appreciate that these recommendations are aimed at improving clarity, accessibility, and presentation, and we have addressed them as detailed below.

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) Table 1

(1a) The description of the column "Promoter Lengths Tested" is a bit confusing because it actually shows acronyms of the used promoters. Suggestion for clarity: either keep the name and mention just the lengths, or rename to "Promoter abbreviation" or "Promoter acronym".

We thank the reviewer for pointing this out. To avoid confusion, we have renamed this column “Promoters Tested”, which better captures the information presented. The column contains both promoter identifiers and the corresponding promoter lengths, which are further clarified in the table notes.

(1b) It is not entirely clear based on the formatting of the table, which columns are relevant for "Blastocystis ST4-WR1" and which for "Blastocystis ST7-B".

We thank the reviewer for this helpful suggestion. We have revised the formatting of Table 1 to more clearly distinguish the data corresponding to Blastocystis ST7-B and Blastocystis ST4-WR1. Specifically, we have added a vertical divider between the relevant column groups to improve readability and make the species-specific information easier to follow.

(2) Figure 2:

If the authors wish to preserve the decorative colouring in the parts B and C, it would be better to at least keep the datapoint and boxplot hues consistent for individual conditions (or plot the datapoints in the same, neutral hue throughout, e.g., black or grey). Currently, this is only the case in the part C, but not in the part B.

We thank the reviewer for this useful suggestion. We have revised Figure 2B to improve visual consistency between the data points and boxplots while preserving the overall colour scheme of the figure. This adjustment improves readability without changing the data or its interpretation.

(3) Figure 3: With the modifications everything is clear. However, two issues are now apparent.

(3a) After the part A was modified, the arrow colours changed (had been yellow and red, now are cyan and magenta), but the description in the legend remained (yellow and red), so the text should be corrected. [By the way, the original colours worked well.]

We apologise for overlooking this inconsistency. The Figure 3 legend has now been corrected to match the revised arrow colours in panel A.

(3b) The care taken by the authors to make the images more accessible is really greatly appreciated, but being a person on the colourblind spectrum, I can attest that the issue is not always just about red and green discrimination: the greyscale and blueish green used in the part A photo in particular are discernible only at huge magnification (to some people). If the signal in the part A were of the same hue as in the part B (yellowish green instead of blueish green), it would readily pop out. For that matter, what is the reason for the use of a different colour profile of the UnaG fluorescence in these two images?

We sincerely thank the reviewer for this important accessibility-related comment. The difference in colour profiles between panels A and B was intentional because the images were acquired using different imaging modalities, as indicated in the figure legend. We wanted to avoid implying that the two panels were generated under identical imaging conditions. However, we appreciate the reviewer’s point that this distinction should not come at the expense of readability. We have therefore adjusted the display of the UnaG signal in panel A to improve contrast and visibility. 

(4) Conclusion:

The expression "bringing endogenous regulatory part discovery, namely the identification of native promoter and terminator elements" feels a bit clunky. What the part "endogenous regulatory part discovery" alludes to is now clearer, but consider reformulating it to "discovery of endogenous regulatory elements". This would make it clear without the need to add the explanation "namely the identification of native promoter and terminator elements". [It is now clear that the accumulation of noun adjectives and the significance of the word "part" was what originally blurred the overall meaning.

We thank the reviewer for this valuable suggestion. We agree that the original phrasing was unnecessarily clunky and have revised the sentence for clarity and flow. Lines 682–684 now read:

“By integrating endogenous promoter and terminator discovery, DNA delivery, selection, clonal recovery, and reporter validation into a single pipeline, we provide a flexible foundation for routine transgene-based studies.”

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This is an interesting study that addresses whether mitochondrial DNA (mitoDNA) variants impact telomere length (TL), which may be relevant to potential maternal inheritance of TL in offspring. The study addresses this question using a cybrid model approach in which mitochondria from donor platelets from 7 individuals that vary in TL and differ in mitoDNA variants are introduced into 143B cells that lack mitochondria. MitoDNA variants that exhibited reduced complex I activity showed telomere shortening in cybrids and increased telomere dysfunction. Interestingly, these phenotypes could be reduced with NAC antioxidant and NAD+ supplementation, suggesting that ROS and oxidative DNA damage at telomeres contributed to the telomere shortening. They further showed that cybrids with lower levels of ROS correlated with longer TL in the lymphocytes of the mitochondrial donors.

Strengths:

This study provides compelling evidence that mtDNA variants influence TL through a mechanism involving mitochondrial-derived ROS, potentially causing telomeric oxidative damage. The data are robust, and the manuscript is well written. However, the study could be strengthened by addressing the following questions and minor weaknesses below.

We thank the reviewer for this very positive evaluation of our work.

Weaknesses:

(1) Introduction. Line 81, the relationship between TL and the risk of lymphoid and myeloid leukemia is not straightforward. POT1 variants associated with long TL increase the risk for lymphoid and myeloproliferative neoplasms (see PMID: 41564438 for example).

We appreciate the reviewer raising the important link between pathogenic POT1 variants and lymphoid malignancies driven by elongated telomeres. We would like to clarify, however, that our introduction focused not on the pathological telomere attrition characteristic of telomere biology disorders, but rather on the natural, non-pathological variations observed in individuals with baseline telomere lengths on the shorter end of the spectrum.

Nevertheless, the two following publications by the Armanios lab have been added in the introduction to underscore the complex relationship between telomere length and tumorigenesis:

DeBoy EA et al. Familial clonal hematopoiesis in a long telomere syndrome. 2023. N Engl J Med 388, 2422-2433.

Davidson-Swinton HR et al. Lymphoid malignancy and clonality in the POT1-mediated long telomere syndrome. 2026. Blood 147, 2226-2237.

Here is the corresponding sentence in the revised manuscript:

“However, some pathogenic mutations in POT1 gene, linked to very long telomeres, were also previously associated with increased risk for lymphoid and myeloproliferative neoplasms (5,6), underscoring the complex relationship between TL and cancer predisposition.”

(2) Figure 1. Since sex also influences TL, it would be good to know the sex of the selected individuals or explain why this is not necessary.

Because this study investigated the potential maternal inheritance of TL via the mitochondrial genome, our cohort consisted predominantly of female donors (6/7). Donor #5, the husband of Donor #7, was the only male included. We have added the information in the text:

“All were of European origin, thus excluding a possible bias linked to African ethnic groups (7), and the seven donors belonged to distinct mitochondrial subhaplogroups (Fig 1D). All but one (#5) were female donors.”

Notably, our analysis revealed minimal influence of sex on TL, which cannot account for the observed differences between the extreme groups.

(3) Please include a description of the 143B cells that were used for cybrid formation in the Results section when introducing the cybrids.

We did it:

“To evaluate the impact of distinct mitochondrial genomes on TL in human cells, we used a transmitochondrial cybrid strategy in which mtDNA-depleted Rho⁰ (ρ⁰) cells, derived from 143B human osteosarcoma cancer cells, are fused with donor platelets, thereby restoring functional mitochondria carrying donor-specific mtDNA variants (21).”

(4) Lines 155-156. The authors note that cybrids from donors 1 and 2 show "pronounced" telomere damage. This result indicates an increase in 53BP1-positive telomeres, which could be indicative of telomere dysfunction or damage. Quantification of the increased chromosome end fusions for cybrids 1 and 2 would strengthen the result.

We thank the reviewer for this suggestion. Following their advice, we used our metaphase spread FISH analyses to quantify chromosome end fusions in the parental 143B Rho0, Cyb1 and Cyb6 cells. However, because Cyb2 metaphase spreads were of insufficient quality for adequate chromosome analysis, we restricted our telomere fusion comments exclusively to Cyb1 and included the quantifications in our revised manuscript (Fig 2E).

Do the increased fusions correlate with an increase in telomere signal-free ends? These should be apparent in the telomere FISH images of metaphase chromosomes.

While this is a strong argument, the telomeres within these cybrid models are critically short. Consequently, the FISH signal intensity falls below the threshold required for reliable quantification of telomere-free ends.

(5) Lines 168-169. What is the evidence that the "in vitro metabolic shift" causes acute oxidative stress?

The reviewer is correct that we have not formally demonstrated this in our experimental system. Instead, our assumption was based on the fact that the initial phase of Rho0 cell repopulation involves a temporary ROS burst, partly driven by incompletely assembled ETC supercomplexes that are known to elevate ROS levels (Maranzana et al., 2013). This is supported by our experimental observation that the NAC antioxidant, combined with NR, potently inhibits telomere shortening in cybrids with low CI activity. We added the following sentence in the revised manuscript:

“When mitochondria are replenished in ρ⁰ cells during the formation of transmitochondrial cybrids, a shift from glycolysis to OXPHOS occurs (Fig S4A-B) and cells need to adapt to this metabolic change. Notably, the initial phase of ρ⁰ cell repopulation involves a temporary ROS burst, partly driven by incompletely assembled ETC supercomplexes that are known to elevate ROS levels (22).”

(6) Why did the elevated ROS in cybrid #3 (Figure 4C) not translate to shorter telomeres in the cybrid (Figure 2A)? Perhaps there is a difference between factors that determine TL in the cybrid vs the donor's lymphocytes?

We cannot fully explain the discrepancy, but we indeed suspect in vivo oxidative stress differs significantly from cell cultures (21% O₂). Additionally, early cybrid replenishment involves an unknown telomere elongation step that may offset mitochondrial ROS-induced shortening.

To further investigate this question, we measured telomere length across varying population doublings (PDs) and observed the following shortening after 66-67 PDs:

- Cyb3: about 1.6 kb reduction

- Cyb6: about 1.2 kb reduction

- Cyb7: about 0.8 kb reduction

These results suggest that the rate of telomere shortening in culture may be higher in Cyb3 cells, possibly due to increased ROS levels.

We included these results as Supplementary Figure 7 and have discussed these data in the revised manuscript:

“Consistently, tracking TL over sequential population doublings revealed that Cyb3 cells are more vulnerable to progressive telomere shortening than Cyb6 or Cyb7 cells (Fig S7). Together, these findings support a role for mitochondrial ROS in human TL regulation.”

In Figure 4B, it appears that the statistical comparisons for mitochondrial superoxide are all relative to Cyb3. If so, why are the comparisons not with the parental 143B rho0 cell line? Please clarify.

We excluded Rho0 cells from our superoxide measurements because these cells were grown in a different culture medium. Instead, we focused on comparing mitochondrial ROS across cybrids to accurately correlate these values with the telomere length of the corresponding donors’ lymphocytes. Consequently, Rho0 cell measurements would not have contributed to this correlation analysis.

We have discussed this in the revised manuscript:

“Mitochondrial superoxide production was measured by electron paramagnetic resonance (27) in clones #1 of all cybrids and in 143B cells (Fig 4B). We excluded 143B ρ⁰ cells from our superoxide measurements because these cells were grown in a different culture medium.”

(7) Given the heterogeneity in TL and mtDNA variants in the human population, the conclusions could be further strengthened by increasing the number of donors and cybrids analyzed. However, there are admittedly practical factors. Overall, these findings are compelling and provide a solid foundation for expanding this analysis in the future. This is more of a comment than a weakness.

We thank the reviewer for this constructive feedback and entirely agree that including more donors would have added depth to our findings. While we acknowledge this limitation, pursuing this further is currently impossible without acquiring new ethical approvals and establishing fresh collaborations with clinicians.

Reviewer #2 (Public review):

Summary:

The authors aim to determine whether mitochondrial genotype influences telomere length. By generating cybrids harboring different mitochondrial backgrounds, the authors seek to establish a mechanistic link between mitochondrial status and telomere biology.

Strengths:

A major strength of the study is the use of cybrid technology, which provides a great approach to investigate the role of mitochondrial DNA independently of the nuclear genome. The authors also employ multiple complementary assays to assess telomere-related phenotypes associated with mitochondrial dysfunction. Together, these experiments generate an interesting dataset that will be of value to researchers interested in the intersection between mitochondrial biology, genome stability, aging, and development. These results also build on previous work supporting roles for ROS/mitochondria in driving telomere shortening.

We thank the reviewer for this very positive evaluation of our work.

Weaknesses:

The data support the conclusion that mitochondrial background is associated with differences in telomere length and telomere-related phenotypes. However, some of the mechanistic interpretations would benefit from additional evidence. In particular, the manuscript discusses mitochondrial influences on telomere shortening, yet telomere length in some experiments is assessed at a single time point. Consequently, the current data do not directly address the rate of telomere attrition. Differences observed between cybrid lines could potentially arise from events occurring during cybrid formation, clonal selection, or subsequent cell expansion. Longitudinal analyses across multiple passages, ideally beginning immediately after cybrid generation and controlling for population doublings, would help establish whether mitochondrial function directly affects telomere shortening dynamics. Some experimental results would also benefit from additional quantification, clarification, and some biological replicates are missing.

We limited our TL measurements to the earliest viable time point after cybrid formation to avoid the confounding effects of cellular adaptation in culture. For instance, the early telomere shortening observed in Cyb1 and Cyb2 cells was later alleviated—likely due to the upregulation of the NAD+ salvage pathway genes NAMPT and NAPRT1. To accurately capture the effects specific to cybrid formation, we isolated 4 independent clones per donor, all of which showed highly consistent TL values, as shown in Figure 2A and S3D.

While we acknowledge the reviewer's point about multi-passage longitudinal analyses, we did, in fact, measure telomere length across varying population doublings (PDs) in Cyb3 (high mito ROS levels), Cyb6 and Cyb7 (moderate to low mito ROS levels) and observed the following shortening after 66-67 PDs:

- Cybrid 3: about 1.6 kb reduction

- Cybrid 6: about 1.2 kb reduction

- Cybrid 7: about 0.8 kb reduction

These results suggest that the rate of telomere shortening in culture may be higher in Cyb3 cells, possibly due to increased ROS levels.

We included these results as Supplementary Figure 7 and have discussed these data in the revised manuscript:

“Consistently, tracking TL over sequential population doublings revealed that Cyb3 cells are more vulnerable to progressive telomere shortening than Cyb6 or Cyb7 cells (Fig S7). Together, these findings support a role for mitochondrial ROS in human TL regulation.”

We have also carefully edited the manuscript so as to clarify the text and, whenever possible, have added quantifications. Among others, as suggested by Reviewer #1, we added the quantification of chromosome end fusions in the parental 143B Rho0, Cyb1 and Cyb6 cells in our revised manuscript:

Author response image 1.

Overall, this study provides interesting evidence linking mitochondrial background to telomere biology. The cybrid models represent a useful resource for the field, and the work raises important questions regarding mitochondria-telomere communication.

Reviewer #3 (Public review):

Strengths:

Mahieu and colleagues address an interesting and underexplored question: whether non-pathogenic variation in the mitochondrial genome contributes to the inter-individual variability of human telomere length (TL). Using a Belgian Flow-FISH reference cohort (n=491) to identify donors at TL extremes, they generate trans mitochondrial cybrids from platelets of seven donors of distinct mtDNA subhaplogroups and characterize the resulting cells with a broad and well-executed toolkit (TRF, TeSLA, ddTRAP, EPR-based mitoROS, Seahorse with permeabilized-cell ETC dissection, LC-MS metabolomics, telomeric PARFISH). The most compelling finding is that cybrids derived from donors with low complex I (CI) activity undergo rapid telomere shortening during the glycolysis-to-OXPHOS transition of cybrid formation, and that this is largely prevented by co-treatment with NAC and the NAD⁺ precursor nicotinamide riboside, supporting a model in which CI sustains the NAD⁺ pool required for PARP1-mediated repair of oxidative damage at telomeres. The authors further report an inverse correlation between donor lymphocyte TL and mitoROS in the corresponding cybrids, and provide preliminary evidence that the K1a-defining ATP6 A177T variant (m.G9055>A) may be enriched in long-telomere individuals.

We thank the reviewer for this very positive evaluation of our work.

Weaknesses:

(1) Statistical support and donor sampling for the central in vivo correlation (Figure 4C).

The inverse correlation between donor lymphocyte TL and cybrid mitoROS (R²=0.794, p=0.007) is the principal in vivo claim of the paper, but it is built on seven donors deliberately selected from the extremes of the Flow-FISH distribution. Sampling at the tails of the outcome variable can substantially inflate apparent correlation strength and significance. I would encourage the authors to (i) explicitly state this sampling structure where the correlation is introduced, (ii) report a leave-one-out sensitivity analysis to confirm the relationship is not driven by one or two donors (Cyb3 and Cyb6 appear to anchor the line), and (iii) where feasible, extend the analysis to additional donors with intermediate TL to test whether the relationship holds across the full distribution. Even a modest expansion (e.g., 4 to 5 additional donors at P25 to P75) would substantially strengthen this central claim.

We thank the reviewer for this insightful comment. We have conducted the requested leave-one-out analysis:

- removing Cyb3: R²=0.730; p=0.0302

- removing Cyb6 : R²=0.782 ; p=0.0194

- removing Cyb1 : R²=0.740; p=0.0278

While we agree that additional donors would enhance the study, further experiments are however currently impossible without new ethical clearances and additional clinical partnerships.

(2) Reconciling the cybrid CI / TL relationship (Fig 3B) with the absence of a CI / TL relationship in donor lymphocytes (Figure 4A).

Figure 3B shows a strong correlation between CI activity and TL in cybrids (R²=0.87), while Figure 4A shows no correlation between donor CI activity (measured in the same cybrids) and donor lymphocyte TL. The authors acknowledge this, but the manuscript subsequently builds toward a CI-centric model of in vivo TL regulation, which seems to outrun the data. The most internally consistent interpretation is that the cybrid CI phenotype reports a sensitized in vitro response to the acute oxidative stress of the metabolic shift, rather than a steady-state determinant of leukocyte TL. I would suggest reframing the abstract, significance statement, and Discussion to make this distinction clearer. The in vitro CI / NAD⁺ / PARP1 axis is a strong finding on its own, while the in vivo role of CI activity (as opposed to ROS more broadly) is not yet established here. Donor #1's profile (very long lymphocyte TL, low CI activity, severe shortening in cybrids, no telomere inheritance in offspring) is informative in this regard and could be discussed more directly as a case that helps delineate where the cybrid model does and does not recapitulate in vivo biology.

We acknowledge that our study does not establish the in vivo role of CI activity in TL regulation. Our abstract specifically highlights an in vitro phenomenon: “Under the specific conditions of cybrid formation, which involve a metabolic shift from glycolysis to oxidative phosphorylation, mtDNA variants associated with reduced CI activity induced rapid telomere shortening, …”.

We nevertheless extensively revised the Abstract/Significance Statement to clearly separate our in vitro results from in vivo biology as requested:

“Abstract

Telomere shortening is a hallmark of aging, yet telomere length (TL) varies considerably among individuals and is strongly influenced by inheritance. In mice, efficient mitochondrial function, characterised by low reactive oxygen species (ROS) production, is critical for telomere elongation during early embryogenesis. Since mitochondrial DNA (mtDNA) encodes several subunits of the electron transport chain, it may influence TL at birth by regulating mitochondrial function in utero. To explore the relationship between mtDNA and TL in human, we used a transmitochondrial cybrid approach, introducing mitochondria from donor platelets with varying telomere lengths into mtDNA-depleted cells. This revealed an inverse correlation between donor blood TL and mitochondrial ROS levels measured in the resulting cybrids, suggesting that specific mtDNA variants may contribute to the maintenance of long telomeres in humans by enhancing mitochondrial fitness. During in vitro cybrid formation, a transient phase of oxidative stress precedes cellular adaptation. In this specific window, mtDNA variants associated with reduced complex I (CI) activity induced rapid telomere shortening—an effect rescued by antioxidant and NAD⁺ precursor supplementation. While these variants occur naturally in certain individuals with long telomeres, our data suggest that, at least under in vitro conditions of acute oxidative stress, CI is critical to support PARP1 activity by maintaining the NAD⁺/NADH balance, thereby preserving telomere integrity. Collectively, these findings solidify the link between mtDNA variants and human TL regulation, highlighting potential therapeutic opportunities for mitochondrial replacement strategies.”

“Significance Statement

“Telomere length at birth influences aging trajectories and disease risk later in life, yet the mechanisms governing this trait remain incompletely understood. Using a trans mitochondrial cybrid approach, we show that single-nucleotide variants in the mitochondrial genome of healthy donors directly affect mitochondrial metabolism and reactive oxygen species production. In addition, mitochondrial ROS levels measured in cybrids inversely correlate with blood cell telomere length in donors. During cybrid formation, mitochondrial DNA variants associated with reduced CI activity promote telomere shortening. Attrition was reversed by antioxidant and NAD⁺ precursor supplementation, pointing to an essential role for robust CI function in sustaining telomere length during acute oxidative stress, at least under in vitro conditions. Together, these findings establish a direct link between mitochondrial genetics, redox homeostasis, and telomere maintenance in human cells.”

Overall, the manuscript has also been carefully edited to account for this comment.

(3) The K1a / ATP6 A177T inheritance claim.

The proposal that K1a (and specifically ATP6 A177T) contributes to maternal inheritance of long telomeres is intriguing but currently rests on three pedigrees (one of which, donor #1, does not support the hypothesis) and a chi-square test that does not reach significance (p=0.153, Figure 4F). The supporting evidence is also limited by the fact that platelet-mediated mitochondrial transfer delivers donor mitochondrial proteins, lipids, and residual mtRNA in addition to mtDNA, making it difficult to attribute the cybrid phenotype of donor #6 specifically to the ATP6 A177T variant. I would recommend either: (a) extending the genotyping screen to additional unrelated donors and, if feasible, confirming the effect of ATP6 A177T through an isogenic approach (e.g., mtDNA base editing in a clean background), or (b) softening the relevant statements to "suggestive trend warranting larger studies," and presenting the K1a observation as hypothesis-generating rather than supportive. The Ashkenazi-centenarian connection raised in the Discussion is an excellent direction for follow-up and could be framed accordingly.

We agree that the evidence for the AT6 A177T inheritance claim remains inconclusive. To clarify, we do not argue that this mitochondrial variant is solely responsible for longer telomeres; indeed, the mtDNA genome of donor #1 suggests otherwise. Furthermore, the phenotypic impact of such mtDNA variants likely depends on nuclear variants in other telomere-related genes (e.g., hTERT or hTR), meaning AT6 A177T may not consistently result in elongated telomeres. Unfortunately, our ethical protocol precludes screening additional unrelated donors. We have revised the text to soften our statements accordingly.

New references:

DeBoy EA et al. Familial clonal hematopoiesis in a long telomere syndrome. 2023. N Engl J Med 388, 2422-2433.

Davidson-Swinton HR et al. Lymphoid malignancy and clonality in the POT1-mediated long telomere syndrome. 2026. Blood 147, 2226-2237.

Maranzana E et al. Mitochondrial respiratory supercomplex association limits production of reactive oxygen species from complex I. 2013. Antioxid Redox Signal 19, 1469-1480.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Figure 3C. Please clarify. Do the first two bars represent NAMPT, and bars 3-4 represent NAPRT1?

We thank the reviewer for pointing this out, and we have fixed the problem.

Reviewer #2 (Recommendations for the authors):

The authors discuss telomere shortening throughout the manuscript, but telomere length is measured only at a single time point. It would be more informative to pass the cells over several population doublings and determine the rate of telomere shortening. Longitudinal analysis across multiple passages, ideally starting immediately after cybrid generation and controlling for population doublings, would be required to determine whether mitochondria directly influence telomere attrition rates. Overall, I like the manuscript- I think it is interesting and impactful, but some controls are missing.

We thank the reviewer for this positive evaluation of our work and have inserted the TRF results of our longitudinal analysis of telomere length in Cybrids #3 (high ROS), #6 (low ROS) and #7 (very low ROS) cultured until PD 66-67 after cloning. Data are shown as Fig S7.

We observed the following shortening after 66-67 PDs:

- Cyb3: about 1.6 kb reduction

- Cyb6: about 1.2 kb reduction

- Cyb7: about 0.8 kb reduction

These results suggest that the rate of telomere shortening in culture may be higher in Cyb3 cells, possibly due to increased ROS levels.

(1) Why would rho (0) have shorter telomeres than parental cells? Or decreased telomerase activity?

We will look at this soon. Our current hypothesis, based on the recent work by the Agarwal’s lab, is that the short telomeres in 143B Rho0 cells happen because these cells lack the nuclear-encoded TK1 enzyme and cannot make pyrimidines through the salvage pathway or de novo (since dihydroorotate dehydrogenase needs working mitochondria). When mitochondria return, thymidine levels may rise and help telomerase work again, potentially through an allosteric mechanism as previosuly suggested (Mannherz and Agarwal, Nat Genet 2023).

This was already discussed in our manuscript (Discussion):

“Our study also unexpectedly revealed a reduction in telomere length in 143B cells following mitochondrial depletion. This telomere shortening was associated with decreased telomerase activity, as measured by ddTRAP, but not with reduced expression of the telomerase subunits hTERT or hTR. 143B osteosarcoma cells are deficient in thymidine kinase 1 and therefore lack an effective pyrimidine salvage pathway. In the absence of oxidative phosphorylation, the de novo thymidine synthesis pathway is also compromised, rendering 143B r⁰ cells dependent on uridine supplementation for survival. Although this hypothesis requires further investigation, we propose that the shorter telomeres observed in 143B r⁰ cells may be linked to the emerging role of thymidine nucleotide metabolism in the regulation of human telomere length, potentially through an allosteric effect of dTTP on telomerase activity (4143).”

(2) Why does 2C data show no variation? How many biological replicates?

We showed hTR and hTERT expression levels in one biological replicate of two independent cybrid clones from each donor, with technical replicates for each measurement. Measurements of hTERT and hTR expression levels over successive PDs were performed for some clones and showed good consistency.

(3) Why did the TIF analysis not compare parental and Rho (0) cells?

We have now added the data in Fig 2D.

Figure 2E is only a representative image; no quantification is provided, so no conclusions about fusion can be made.

We have now quantified chromosome end fusions in the parental 143B Rho0, Cyb1 and Cyb6 cells and have included the quantifications in our revised manuscript (Fig 2E):

“E. Left: Visualisation of telomere fusions (white arrowheads) in Cyb1 cells at PD7. 143B r⁰ and Cyb6 cells are shown as controls. Telomeres are detected by FISH (red) and DAPI stains DNA (blue). Scale bar: 5 µm. Right: Quantification of telomere fusions. The total number of analyzed chromosomes is shown for each cell line. Χ² test. ns: p>0.05.”

(4) In Figure 3, I found it difficult to interpret the data shown in D (what is each lane?).

Each lane shows TL of an independent hybrid clone. We have clarified the legend accordingly.

Why is the data in E shown this way? How many biological replicates, and why no experimental validation?

Panel E quantifies the TRF analyses conducted on independent cybrid clones. These clones were isolated from new cybridizations of donor 2’s platelets with 143B Rho0 cells under the specified conditions. The specific number of independent cybrid clones (which we consider as biological replicates) for each condition is shown in the graph: NAA: 5, NAC: 7, NAC + NR: 8, NAA + NR: 8. We have clarified the legend as follows. We hope this is clearer now.

“E. Quantification of the TRF analyses conducted on independent cybrid clones isolated in the conditions detailed in D. The percentage of clones with average TL>2.5 kb was calculated. The specific number of independent cybrid clones analyzed for each condition is shown in the graph: NAA: 5, NAC: 7, NAC + NR: 8, NAA + NR: 8.”

(5) Did NAC and NR also reduce TIF or telomere fusions?

We did not test this. We expect NAC/NR treatment to reduce TIF and telomere fusions indeed.

For the Parylation experiments, how many independent experiments were performed?

Eight independent cybrid clones obtained from 4 independent cybridisations were analyzed. This has now been detailed in the legend as follows :

“F. Representative images and quantification of telomeric parylation in 8 independent Cyb2 clones obtained from 4 independent cybridisations, comparing cells that did or did not exhibit telomere shortening during the initial PDs following cybridisation (from panel D-E).”

(6) Figure 4. Why were mitochondrial superoxide levels not measured in parental cells?

We excluded Rho0 cells from our superoxide measurements because these cells were grown in a different culture medium. Instead, we focused on comparing mitochondrial ROS across cybrids to accurately correlate these values with the telomere length of the corresponding donors’ lymphocytes. Consequently, Rho0 cell measurements would not have contributed to this correlation analysis.

We have discussed this in the revised manuscript:

“Mitochondrial superoxide production was measured by electron paramagnetic resonance (24) in clones #1 of all cybrids and in 143B cells (Fig 4B). We excluded 143B r⁰ cells from our superoxide measurements because these cells were grown in a different culture medium.”

Reviewer #3 (Recommendations for the authors):

Additional analyses for Figure 4C. Please report a leave-one-out sensitivity analysis for the lymphocyte TL versus cybrid mitoROS correlation,

We have conducted the requested leave-one-out analysis:

- removing Cyb3: R²=0.730; p=0.0302

- removing Cyb6: R²=0.782; p=0.0194

- removing Cyb1: R²=0.740; p=0.0278

We chose not to include this analysis in the revised manuscript.

and state in the legend that donors were selected at the extremes of the Flow-FISH distribution.

This is not exactly the case, but we nevertheless added this sentence in the legend:

“TL in the donor lymphocytes was distributed as follows: >P90 (#1, #6 and #7), around P50 (#2 and #4), between P10 and P50 (#5) and at P10 (#3).”

If feasible, extend the analysis to 4 or 5 additional donors with intermediate TL (P25 to P75) to test whether the relationship holds across the full distribution.

While we agree that additional donors would enhance the study, further experiments are however currently impossible without new ethical clearances and additional clinical partnerships.

Reframing of the in vivo claims. Please calibrate the language in the abstract, significance statement, and Discussion so that the in vitro complex I / NAD⁺ / PARP1 mechanism and the in vivo role of the mitochondrial genome are presented at the appropriate levels of evidence. A brief paragraph in the Discussion explicitly addressing donor #1 (long lymphocyte telomeres, low complex I activity, telomere shortening in cybrids, no inheritance of long telomeres in offspring) would be helpful in delineating where the cybrid model does and does not recapitulate in vivo biology.

The text has been thoroughly revised in accordance with this suggestion. We kindly invite you to review the updated manuscript for full details.

Strengthening the K1a / ATP6 A177T claim. Two options would address the concern raised in the public review. First, extending the genotyping screen to additional unrelated donors until the chi-square test reaches the level of evidence consistent with the wording in the abstract.

Unfortunately, further experiments are currently impossible without new ethical clearances.

Second, if a collaboration is available, an isogenic introduction of the m. G9055>A variant in a clean mitochondrial background through mitochondrial base editing or mitoTALENs would directly test causality.

This would certainly be an excellent approach to test causality indeed and we fully agree that future collaborations with specialized labs would be highly relevant in this context.

If neither is feasible, please soften the statements to a suggestive trend warranting larger studies.

We chose to soften our claims instead; please see the revised manuscript for details.

Direct test of PARP1 involvement. A PARP1 knockdown or a PARP inhibitor co-treatment in Cyb2 during fusion would directly test whether the NAC + nicotinamide riboside rescue depends on PARP1 activity, as the model proposes. If this experiment is not feasible, please state so in the Discussion.

Again, redoing cybridisations is currently impossible without new ethical clearances. We nevertheless acknowledge that the suggested experiment is interesting and we discussed it in the revised manuscript as follows:

“Mitochondrial platelets with low CI activity triggered significant telomere shortening in recipient cells during early cybrid formation -a loss that was prevented by co-treatment with an antioxidant and an NAD⁺ precursor. Although we did not determine whether the rescue was dependent on PARP1, these results support the essential role of CI in maintaining PARP1 activity via regulation of the NAD⁺/NADH balance.”

Figure 1C/D legend says "eight selected donors" twice (lines 635, 636), but the text says "seven donors" (lines 132, 258), and donors are numbered #1-#7 throughout. This is a real internal inconsistency in the manuscript that the authors should fix.

We have fixed this mistake. Thanks for bringing this to our attention.

Author response:

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

eLife Assessment:

This study presents a valuable investigation of how inhibition of the WNK-SPAK/OSR1 pathway influences neuronal chloride homeostasis and seizure-like activity in organotypic hippocampal slice cultures. The evidence supporting the principal mechanistic conclusions is incomplete because several proposed mechanisms are inferred from changes in chloride dynamics rather than directly demonstrated. The work will be of interest to researchers studying chloride homeostasis, inhibitory neurotransmission, and epilepsy.

We appreciate the thoughtful reviews and assessment. Additional data analysis has been performed, and the paper has been carefully modified to address each concern, as described below.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors used extracellular field potential recordings and two-photon imaging to monitor neuronal network activity and intracellular chloride concentration ([Cl-]i) in organotypic hippocampal slices from mice expressing the genetically encoded chloride fluorophore Clomeleon. These slices were used as a model of acute traumatic brain injury and epileptogenesis in vitro. The study provides evidence that blocking the WNK-SPAK/OSR1 pathway with WNK463 alleviates epileptic activity, and that this anticonvulsant effect involves suppression of the chloride loader NKCC1 and enhancement of chloride extrusion via KCC2. Overall, this is a solid study with a comprehensive pharmacological analysis.

Strengths:

The conclusions are well supported by the detailed pharmacological analysis.

Weaknesses:

The only weakness I see is the absence of cellular-level electrophysiology, which precludes interpretation of the imaging data in the context of GABA action polarity.

The referee correctly points out that we did not perform cellular-level electrophysiological measurements. Before the advent of transgenic ratiometric chloride-sensitive fluorophores, we conducted detailed studies of neuronal cation-chloride transport using electrophysiological measures (Staley and Proctor, 1999). We did not measure membrane potential in the current study because this data is not needed for characterization of cation-chloride membrane cotransport, which is electroneutral. Electroneutral processes are not affected by membrane potential, and electroneutral processes in turn do not alter the membrane potential. We did not measure membrane GABA currents because the polarity of GABA currents was clearly demonstrated by our fluorometric measures of the corresponding increases or decreases in cytoplasmic chloride concentration (Figure 2). We have added the following sentence to the Discussion (Page 16): “In this fluorometric study, we did not measure RMP and E_GABA directly, but rather inferred the impact of electroneutral cation-chloride transport on these parameters from the effects on [Cl^-]_i (Figure 2) and seizure activity (Figures 1, 3-9)”.

Reviewer #2 (Public review):

Summary:

The authors investigate whether inhibition of the WNK-SPAK/OSR1 pathway using the allosteric inhibitor WNK463 improves neuronal chloride homeostasis and suppresses epileptiform activity in organotypic hippocampal slice cultures. Using Super Clomeleon imaging combined with extracellular field recordings, they demonstrate that WNK463 accelerates recovery of intracellular chloride following chloride loading, reduces interictal chloride accumulation, and progressively suppresses recurrent ictal-like discharges. Pharmacological inhibition and siRNA-mediated knockdown of NKCC1 and KCC2 are then used to investigate the contribution of these transporters to the anti-ictal effects of WNK463.

Strengths:

The study addresses an important question in the field of chloride homeostasis and epilepsy and combines complementary experimental approaches. In particular, the distinction between baseline chloride measured in the presence of TTX and activity-dependent interictal chloride accumulation provides a useful conceptual framework for interpreting previous studies of WNK-SPAK inhibition. The imaging, electrophysiological, and pharmacological data are internally consistent and support the conclusion that WNK463 alters chloride dynamics and substantially suppresses ictal-like activity in this model.

Weaknesses:

The principal limitation of the manuscript is that several mechanistic conclusions extend beyond the experimental observations. Throughout the results and discussion, the authors interpret the observed changes in intracellular chloride dynamics as evidence of enhanced CCC-mediated chloride extrusion, while the pharmacological and siRNA-mediated experiments are interpreted as supporting coordinated NKCC1 inhibition and KCC2 activation, ultimately leading to restoration of GABAergic inhibition and negative shifts in EGABA. While these interpretations are plausible and consistent with the data, they remain inferential because transporter phosphorylation or activity, EGABA, and inhibitory synaptic function were not directly assessed in the current study. Moreover, although the pharmacological and knockdown experiments support a contribution of NKCC1 and KCC2 to the actions of WNK463, they do not definitively establish coordinated modulation of both transporters as the primary mechanism underlying seizure suppression. These mechanistic conclusions should therefore be presented more cautiously.

The referee correctly points that we did not definitively establish the link between coordinated modulation of NKCC1 and KCC2 transporter activity, changes in EGABA and GABA function to the anti-ictal action of WNK463. Indeed we have an entire section of results dedicated to the anti-ictal effects of WNK463 that persist after block of NKCC1 and KCC2. The primarily biochemical study by Lee et al (2022) demonstrated that the WNK-SPAK/OSR1 inhibitor WNK463 reduced KCC2-T1007 phosphorylation and EGABA in cultured cortical neurons challenged with high 30 mM [Cl^-]_i in vitro, and limited KA-induced status epilepticus in vivo. We are studying the same system with different pharmacological, electrophysiological, optogenetic and morphological tools during spontaneous ictal-like epileptiform discharges in organotypic hippocampal slices in vitro. We prominently cite the previous study and clearly report new findings and demonstrate underlying mechanisms. We have also modified the language surrounding our conclusions (e.g. last sentence of abstract, and last sentence of first paragraph of Discussion).

The manuscript would also benefit from broader contextualization within the current literature. The introduction largely focuses on previous work from the authors' group and provides a relatively narrow overview of chloride homeostasis in epilepsy. In particular, the discussion would benefit from broader consideration of studies examining KCC2 dysfunction in human epilepsy and experimental models, alternative mechanisms regulating KCC2 activity following seizures, and recent therapeutic strategies targeting KCC2.

We agree. We have added the following paragraph to the Discussion (p. 16-17): “The KCC2 protein is a potassium-chloride co-transporter that maintains low [Cl^-]_i (Rivera et al., 1999). KCC2 dysfunction has been implicated in epilepsy across human and experimental studies. Reduced KCC2 expression and impaired chloride extrusion have been demonstrated in resected tissue from patients with temporal lobe epilepsy, and pathogenic variants in SLC12A5 further support a causal role for impaired KCC2 function in human epilepsy (Huberfeld et al., 2007; Puskarjov et al., 2014). Experimental seizures can suppress KCC2 through several mechanisms in addition to WNK-SPAK/OSR1 signaling, including BDNF-TrkB-dependent downregulation, dephosphorylation of the stabilizing Ser940 site with subsequent internalization, and calpain-mediated proteolysis (Rivera et al., 2004; Silayeva et al., 2015; Puskarjov et al., 2012). These convergent mechanisms suggest that loss of KCC2 function may both result from and amplify seizure activity by weakening GABAergic inhibition. Accordingly, KCC2 has emerged as a therapeutic target: strategies include modulation of regulatory phosphorylation, enhancement of KCC2 expression, and direct pharmacological potentiation. Notably, the KCC2 activator OV350 enhances chloride extrusion and suppresses experimental seizures, including benzodiazepine-refractory status epilepticus, providing proof-of-concept for direct KCC2 activation as an antiseizure strategy (Jarvis et al., 2023).”

Finally, although the authors appropriately acknowledge that the experiments were performed exclusively in vitro, the discussion could more explicitly address the limitations of the organotypic hippocampal slice model, including how culture-induced network reorganization and spontaneous epileptiform activity may influence chloride homeostasis and the extent to which these findings generalize to traumatic brain injury and chronic epilepsy in vivo. In addition, the statistical analysis would benefit from clarification regarding the experimental unit and the treatment of repeated measurements.

Thank you. We addressed the limitation of organotypic hippocampal slices in vitro in the Limitation and Future Directions paragraph (p. 18-19): “Our experiments were conducted in organotypic hippocampal slices in vitro. Advantages of this preparation include homogenous injury and consistent epileptogenesis. This provides excellent control of the extracellular environment and imaging but does not replicate the in vivo vascular supply and maintenance of ionic homeostasis. While we find that increased WNK-SPAK/OSR1-mediated KCC2 activity via enhanced Cl^- extrusion rates robustly reduces seizure activity in vitro, it is possible that in vivo, increased KCC2 activity could lead to extracellular potassium accumulations (Viitanen et al., 2010) that would limit Cl^- extrusion independently of the velocity of KCC2 transport (Thompson et al., 1988; Staley and Proctor, 1999). Thus, it will be important to assess these findings in vivo.”

We provided better clarification regarding the treatment of repeated measurements (p. 22): “Experimental data were analyzed using a repeated measures ANOVA for two types of study design. Studies that investigated either (1) changes in mean (median) parameters over three or more time points or consecutive time intervals; or (2) differences in mean (median) parameters under three or more different conditions”.

Reviewer #3 (Public review):

Summary:

Dzhala and colleagues present findings from organotypic slice cultures suggesting that simultaneous modulation of the complementary cation-chloride cotransporters NKCC1 and KCC2 through inhibition of the WNK-SPAK/OSR1 pathway reduces seizure-like activity. The manuscript is generally well written, and the data support the conclusion that WNK463 exerts robust anti-ictal effects in this model. However, several issues should be addressed to strengthen the mechanistic interpretation and statistical rigor of the study, and improve confidence in the conclusions.

Strengths:

(1) The study addresses an important mechanistic question by investigating how inhibition of the WNK-SPAK/OSR1 pathway with WNK463 influences seizure activity and neuronal chloride homeostasis.

(2) The experimental design is logical and comprehensive, progressing from characterization of chloride dynamics to pharmacological and genetic interrogation of the underlying mechanism using multiple complementary approaches, including pharmacological inhibition, siRNA-mediated knockdown, electrophysiology, and chloride imaging.

(3) The combination of simultaneous extracellular electrophysiology and two-photon chloride imaging provides complementary functional and mechanistic information and represents a major technical strength of the study.

(4) The TTX experiments elegantly distinguish activity-dependent chloride accumulation from resting intracellular chloride concentration, substantially strengthening the central mechanistic conclusions.

Weaknesses:

(1) The mechanistic conclusions regarding KCC2 activation and NKCC1 inhibition are stronger than the data directly support. Throughout the manuscript, the authors conclude that WNK463 activates KCC2 and inhibits NKCC1. Although this interpretation is consistent with the established biology of the WNK-SPAK/OSR1 pathway, the evidence presented here is indirect. Specifically, the authors infer KCC2 activation and NKCC1 inhibition from the observation that pharmacological inhibition or siRNA-mediated knockdown of these transporters alters the effects of WNK463, together with measurements of chloride dynamics. While these findings are compatible with a KCC2- and NKCC1-dependent mechanism, they do not directly establish that WNK463 regulates either transporter. Direct evidence would require measurements of transporter activity, phosphorylation state, membrane expression, or other biochemical indices of transporter regulation. I therefore recommend that the authors both temper the mechanistic language throughout the manuscript and explicitly acknowledge in the Discussion that the proposed regulation of KCC2 and NKCC1 is inferred from indirect evidence rather than directly demonstrated in the present study.

We agree. We modified the key conclusory sentences in the Abstract and Discussion as described in the response to referee 2. The referee correctly points that we did not directly establish the link between the action of WNK463 and coordinated activation of KCC2 and inhibition NKCC1. We highlighted the established link in the discussion (p. 17-18): “NKCC1 and KCC2 are rapidly stimulated and inhibited, respectively, by direct phosphorylation mediated by the Cl^--sensitive WNK-SPAK/OSR1 complex (Alessi et al., 2014). The WNK family senses changes in the [Cl^-]_i, cell volume, extracellular osmolarity and transduces this information to CCCs (Shekarabi et al., 2017). WNKs stimulate the kinases SPAK and OSR1, which directly phosphorylate and stimulate NKCC1 or inhibit KCC2 (Kahle et al., 2013), providing compensatory and reciprocal regulation between transporters activity to maintain chloride homeostasis and neuronal excitability (Hartmann and Nothwang, 2022). Conversely, inhibiting the WNK-SPAK/OSR1 pathway might be an especially potent strategy to reduce neuronal Cl^- elevation and facilitate neuronal Cl^- extrusion by coincident NKCC1 inhibition and KCC2 activation…” Consistently with the established biology of the WNK-SPAK/OSR1 pathway we found that (p.15): “…WNK463 improved [Cl^-]_i homeostasis, progressively enhanced postictal [Cl^-]_i extrusion rates, reduced ictal duration and abolished recurrent ILDs. Our pharmacological investigations suggest that the powerful anti-ictal effects of WNK463 are mediated by reduced NKCC1 and enhanced KCC2 transport activity...”

(2) The conclusions drawn from the siRNA-mediated knockdown experiments should be interpreted more cautiously. First, it is unclear whether silencing NKCC1 or KCC2 induced compensatory changes in the expression or function of the complementary cotransporter. Given the well-established interplay between NKCC1 and KCC2 in regulating intracellular chloride homeostasis, compensatory adaptations could influence the interpretation of these experiments and should be addressed or acknowledged as a limitation. Second, the sample size for the siRNA experiments appears relatively small. It is unclear how many independent animals contributed slices to each experimental group, making it difficult to assess the degree of biological replication. In addition, effect sizes are not reported. Clarifying the number of biological replicates and reporting effect sizes would improve the rigor of the statistical analysis and increase confidence in these findings.

We agree and now address this in the discussion (p. 17-18): “WNKs stimulate the kinases SPAK and OSR1, which directly phosphorylate and stimulate NKCC1 or inhibit KCC2 (Kahle et al., 2013), providing compensatory and reciprocal regulation between transporters activity to maintain chloride homeostasis and neuronal excitability (Hartmann and Nothwang, 2022). ”

We agree that the sample size for the siRNA electrophysiological experiments is relatively small (n=3-4 slices). We now clarify the number of mice were used per each experimental group (p.19). We provide the n (number of slices) and the number of paired cells in the Results and for every experimental conditions.

(3) The final pharmacological experiments require clarification, as the conclusions appear internally inconsistent. Earlier experiments suggest that the anticonvulsant effects of WNK463 depend on coordinated regulation of both NKCC1 and KCC2. However, in the final experiment, the authors state that simultaneous pharmacological inhibition of NKCC1 and KCC2 does not prevent the anticonvulsant effects of WNK463. In contrast, the accompanying statistical analysis indicates that combined transporter inhibition significantly reduces the effect of WNK463 relative to control conditions. These interpretations appear inconsistent and make it difficult to determine the extent to which the anticonvulsant action of WNK463 depends on NKCC1 and KCC2. The authors should clarify whether simultaneous inhibition of both transporters completely abolishes, partially attenuates, or merely reduces the magnitude of the WNK463 response, and revise the text accordingly. If the effect is only partially attenuated, alternative mechanisms contributing to the anticonvulsant actions of WNK463 should also be considered and discussed.

We agree. Our data demonstrated that WNK463 had no effect in the presence of high concentration of bumetanide (500 µM) that nonspecifically blocks CCCs (NKCC1 and KCC2-3) (Figure 6). In contrast (p. 15): ”Simultaneous inhibition of NKCC1 and KCC2 by the combination of bumetanide (10 µM) and VU0463271 (1 µM) significantly reduced the anti-ictal effects of WNK463 (Figure 9).” The conclusory sentence in the Results indicates (p.15): “These results suggest that the anti-ictal effects of WNK-SPAK/OSR1 inhibitor WNK463 are mainly due to downstream interactions with NKCC1 inhibition and KCC2 activation, with additional effects due to interactions with an unidentified Cl^- transporter (e.g. KCC3) or exchanger, or channel.”

(4) The statistical analysis and reporting require further attention. First, median values should not be reported with standard deviations, as standard deviation describes variability around the mean rather than the median. For non-normally distributed data, the authors should report median values together with an appropriate measure of variability, such as the interquartile range (25th-75th percentile) or another suitable summary. Second, in several instances, ANOVA results are reported using only a single degree of freedom value (e.g., page 6, DF = 53). This is incomplete, as an F statistic is defined by two degrees of freedom: the numerator degrees of freedom (between-group variability) and the denominator degrees of freedom (within-group variability). Reporting statistical results using standard notation (F(df_between, df_within) = F statistic, p = value) would improve clarity and allow proper interpretation of the analyses.

Thank you. Group measures are expressed now as mean ± standard deviation (SD) or median (25%-75%) as indicated. In a one-way RM ANOVA, (DF) represents the between-groups degree of freedom, and (F) represents the F-statistic and reported as F(DF_treatment, DF_residual)=value. In the Friedman RM ANOVA on Ranks, the chi-square statistic was used to assess the differences between the groups. The Tukey Test or Holm-Sidak Test was used for all pairwise comparisons of the responses to the different treatment groups. Please see Statistical Analysis in the Methods section (p.23-24).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I have only minor comments/suggestions.

(1) While [Cl^-]i and ECl are informative parameters, interpreting the GABA driving force and determining whether depolarizing/excitatory GABA actions during seizures or interictal states are alleviated by treatment requires knowledge of the membrane potential and its dynamics during epileptic events. I would recommend including this information if available. Gramicidin perforated-patch recordings (ideally) would substantially strengthen the conclusions, at least for a critical subset of experiments.

Please see our response above. We have added the following sentence to the discussion (page 16): “In this fluorometric study, we did not measure RMP and EGABA directly, but rather inferred the impact of electroneutral cation-chloride transport on these parameters from the effects on [Cl^-]_i (Figure 2) and seizure activity (Figures 1, 3-9)”.

(2) Did the authors observe any signs of cell shrinkage in response to WNK463, or transient cellular swelling during interictal-like discharges (ILDs) and its prevention by WNK463? Given that cytotoxic edema is typically associated with increased tissue light transparency and shrinkage of the extracellular space (e.g., as measured with TMA⁺), this reviewer wonders whether such approaches could be used as a proxy for cell swelling. Tissue edema, which manifests as increased tissue volume, could also be assessed by measuring slice thickness.

These are excellent ideas and cell volume is an area of interest for us, but we would argue that assessment of volume effects are outside the scope of the current 9-figure study. We observed cell volume (transverse area) increases during prolonged ictal-like discharges. This effect was prevented by WNK463 during suppression of ictal-like discharges. However, we did not provide the volume analysis in this paper.

(3) The paper should be corrected for spelling and grammar (e.g., Figure 2 legend: "(b) Linier regression analysis revealed that... " - probably should be "Linear... "?).

Thank you. Corrected.

Reviewer #2 (Recommendations for the authors):

(1) Temper mechanistic statements throughout the manuscript by clearly distinguishing experimental observations from inferred mechanisms and by explicitly framing conclusions regarding coordinated NKCC1/KCC2 modulation, chloride extrusion, EGABA, and restoration of GABAergic inhibition as interpretations supported by, rather than directly demonstrated by, the current data.

We have softened the key conclusory sentences in the Abstract and Discussion as described above. In the introduction, we highlighted the potential of both NKCC1 and KCC2 targeting for control of seizures (p. 2): “Previous studies have demonstrated that inhibition of NKCC1 reduced [Cl^-]_i in injured neurons, enhanced GABAergic inhibition and the efficacy of anticonvulsants (Pond et al., 2006; Dzhala et al., 2008; Dzhala et al., 2024; Nardou et al., 2011; Cleary et al., 2013; Sivakumaran and Maguire, 2016; Soul et al., 2021). Conversely, enhancement of KCC2 activity improved [Cl^-]_i extrusion and control of seizures (Gagnon et al., 2013; Moore et al., 2018; Dzhala and Staley, 2021).”

In the discussion we highlighted the potential of coordinated NKCC1 and KCC2 modulation (p. 17-18): “NKCC1 and KCC2 are rapidly stimulated and inhibited, respectively, by direct phosphorylation mediated by the Cl^--sensitive WNK-SPAK/OSR1 complex (Alessi et al., 2014). The WNK family senses changes in the [Cl^-]_i, cell volume, extracellular osmolarity and transduces this information to CCCs (Shekarabi et al., 2017). WNKs stimulate the kinases SPAK and OSR1, which directly phosphorylate and stimulate NKCC1 or inhibit KCC2 (Kahle et al., 2013). Conversely, inhibiting the WNK-SPAK/OSR1 pathway might be an especially potent strategy to reduce neuronal Cl^- elevation and facilitate neuronal Cl^- extrusion by coincident NKCC1 inhibition and KCC2 activation…”

(2) Expand the introduction and discussion to provide a more balanced overview of the current literature on chloride homeostasis in epilepsy, including alternative mechanisms regulating KCC2 dysfunction and recent therapeutic strategies targeting KCC2.

In the introduction, we highlighted the potential of both NKCC1 and KCC2 targeting for control of seizures (p. 2): “Previous studies have demonstrated that inhibition of NKCC1 reduced [Cl^-]_i in injured neurons, enhanced GABAergic inhibition and the efficacy of anticonvulsants (Pond et al., 2006; Dzhala et al., 2008; Dzhala et al., 2024; Nardou et al., 2011; Cleary et al., 2013; Sivakumaran and Maguire, 2016; Soul et al., 2021). Conversely, enhancement of KCC2 activity improved [Cl^-]_i extrusion and control of seizures (Gagnon et al., 2013; Moore et al., 2018; Dzhala and Staley, 2021).” We did not provide additional references to comply with the word limit. We have added a paragraph and citations (pp. 16-17) to the Discussion to address this issue.

(3) Discuss more explicitly the limitations of the organotypic hippocampal slice model when extrapolating the findings to traumatic brain injury and chronic epilepsy in vivo.

Please see our response above. We discussed the limitation of the organotypic hippocampal slice model in the Limitations and future directions section (p. 18-19): “Our experiments were conducted in organotypic hippocampal slices in vitro. Advantages of this preparation include homogenous injury and consistent epileptogenesis (Berdichevsky et al., 2012). This provides excellent control of the extracellular environment and imaging but does not replicate the in vivo vascular supply and maintenance of ionic homeostasis. While we find that increased WNK-SPAK/OSR1-mediated KCC2 activity via enhanced Cl^- extrusion rates robustly reduces seizure activity in vitro, it is possible that in vivo, increased KCC2 activity could lead to extracellular potassium accumulations (Viitanen et al., 2010) that would limit Cl^- extrusion independently of the velocity of KCC2 transport (Thompson et al., 1988; Staley and Proctor, 1999). Thus, it will be important to assess these findings in vivo.”

(4) Clarify how repeated measurements from individual cells and slices were handled in the statistical analyses, including the experimental unit for each analysis.

We clarified in the methods (p.22): “Experimental data were analyzed using a repeated measures ANOVA for two types of study design. Studies that investigated either (1) changes in mean (or median) parameters over three or more time points or consecutive time intervals); or (2) differences in mean (or median) parameters under three or more different conditions”.

Reviewer #3 (Recommendations for the authors):

(1) The manuscript would also benefit from including statements regarding randomization, blinding (beyond the immunohistochemistry analysis), and any inclusion or exclusion criteria, as these details are increasingly expected to improve transparency and reproducibility.

We agree. Images were blinded for the immunohistochemistry analysis (p. 21) and quantitative analysis of intracellular chloride changes (p. 23). Cells that did not respond to GABA/L-glutamate puff applications (Figure 2) and chloride transients that failed to fit an exponential decay function (p. 5) were excluded from the analysis. All other data generated or analyzed during this study were included in the manuscript.

(2) The duration of baseline recordings prior to drug application should be specified in the Methods.

Thank you. This information included in the Method section (p.19): “Slices were stabilized for 10-20 min in ACSF prior recordings and/or imaging”.

(3) Some wording could be refined for readability. For example, "insignificantly reduced " on pages 8 and 14 would be more appropriately stated as "did not significantly reduce. "

Thank you. Corrected.

(4) The first sentence of the Introduction refers to "anticonvulsant (AED)-resistant seizures. " I suspect the authors intended "antiepileptic drug (AED)-resistant seizures, " as the current wording does not match the acronym.

Thank you. Corrected.

Author response:

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

Public Review:

Reviewer #1 (Public review):

Leukemia-driving NUP98 oncofusion proteins form chromatin-associated biomolecular condensates in the nucleus, and these structures are important for oncogenic transformation. Most NUP98 fusions do not contain domains that mediate the recognition of specific DNA elements. Instead, they entail domains that are important for chromatin regulation. For instance, the NUP98::KDM5A fusion features a fusion of the NUP98 N-terminus with the third PHD domain of the histone demethylase KDM5A. As PHD domains are critical for the recognition of methylated histones without any sequence specificity, it is not clear what controls the condensation and chromatin binding of NUP98::KDM5A, leading to the induction of oncogenic transcriptional programs.

In this work, the authors use a combination of cellular and in vitro studies to show that biomolecular condensation of NUP98::KDM5A is dependent on H3K4me3 binding. Their model proposes that concentration-dependent chromatin-associated condensation of NUP98::KDM5A depends on local densities of H3K4me3 on chromatin and the levels of the fusion oncoprotein. In line with this, the analysis of gene expression data from NUP98::KDM5A-positive AML cells shows a positive correlation between differentially expressed genes and H3K4me3 levels.

This is an interesting manuscript that aims to dissect the molecular mechanisms underlying biomolecular condensation of the NUP98::KDM5A oncoprotein. The work is solid, and the results are well explained and presented in a logical order. However, the study suffers from several weaknesses that if addressed would improve the study.

Major points:

(1) All cellular experiments are performed in settings of transient transfection of NUP98::KDM5A in non-hematopoietic cell types. These conditions are not physiologically relevant, as these cells do not depend on the fusion oncogene. Therefore, any claims about concentration-dependent effects on condensation need to be validated in AML cells that are driven by NUP98::KDM5A. While this may not be possible in primary patient-derived cells, several groups have published AML models of NUP98::KDM5A-driven AML that could be used.

We appreciate the reviewer’s point regarding physiological relevance. Our goal in these cellular microscopy experiments was to dissect the biophysical principles of NUP98::KDM5A (including its mutants) condensate formation under controlled expression levels (concentration). While AML model systems driven by NUP98::KDM5A are available, they do not offer this possibility because of pre-existing NUP98::KDM5A expression. Suspension culture of hematopoietic cells also poses practical challenges for correlative FISH+IF and high-resolution microscopy analysis. We agree that validating our observed behaviors in AML models would be valuable, e.g. by creating HSPC lines with inducible expression of tagged NUP98::KDM5A and its mutants, but such experiments fall outside the scope of the current study. We will add text acknowledging this limitation and clarifying that our mechanistic conclusions are grounded in biophysical principles that should generalize across cell types.

In the revised manuscript, we have added a section on study limitations at the end of the discussion section:

Study limitations: Cellular experiments in this study were performed using transient transfection of WT NUP98::KDM5A and its mutants in HEK293 and U2OS cells. While these non-hematopoietic cell models limit physiological relevance, they allowed for controlled expression levels in the absence of endogenous oncofusion and the ease of imaging, enabling investigation of the biophysical principles of condensate formation, the main objective of our study.

(2) The results presented in Figure 4 are not entirely supportive of the mechanism. It is known that active gene expression correlates with high H3K4me3 levels; therefore, the correlations shown by the authors are expected. Yet, the authors do not discuss the fact that many H3K4me3-positive genomic regions do not show NUP98::KDM5A binding. This should be elaborated on in the discussion section.

We agree that active transcription correlates with H3K4me3, and that this baseline relationship must be considered. Our analysis explicitly uses fold-change between patient cells and healthy controls as the readout. This comparison inherently accounts for the activating effect of H3K4me3 itself. Regarding the reviewer’s comment that “many H3K4me3-positive genomic regions do not show NUP98::KDM5Abinding”, we would like to clarify that this point is exactly what our manuscript aims to explain. Our cell line studies show that, at patient-relevant expression levels, NUP98::KDM5A condensates form preferentially at H3K4me3 loci with high local mark density. Considering that NUP98::KDM5A concentration in the nucleus is lower than the KD between KDM5A PHD3 and H3K4me3, this means that H3K4me3 loci with lower mark density will not see NUP98::KDM5A binding without the high local concentration of the fusion protein (as a result of condensate formation). This is consistent with our observation that genes with the highest local density show disproportionately stronger upregulation.

We have modified the final paragraph of the section describing our analysis of gene expression in patient samples to add:

Importantly, to account for the activating effect of H3K4me3 itself, our analysis explicitly uses fold-change between patient cells and healthy controls as the readout.

(3) While the focus of the manuscript is on NUP98::KDM5A, this oncofusion is part of a family of >30 fusions that join the NUP98 N-terminus to a variety of factors with roles in epigenetic control and transcription. While the repertoire of NUP98 fusion partners is diverse with regard to functional domains, they all induce a conserved set of target genes that is characteristic of this leukemia subtype. How can this be achieved in the context of NUP98 fusion proteins that do not contain a PHD domain, such as NUP98::NSD1 or NUP98::HOXA9? Please discuss this.

We appreciate this important conceptual question. Many NUP98 fusions, despite diverse partner domains, produce similar transcriptional programs. Our current hypothesis is that the highly active status of the HOX cluster genes in HSPC attracts NUP98 oncofusions targeting H3K4me3 (e.g., KDM5A and PHF23), while NUP98::HOXA9 and other transcription factor fusions directly target the HOX cluster via DNA sequence recognition. This convergence and the broad targets of the dysregulated HOX transcription factors explain the transcriptional program similarity, sustained by the previously described enrichment of transcriptional co-activators by NUP98 oncofusion condensates. Of note, while several fusion partners of NUP98 lack PHD domains, the NUP98::NSD1 oncofusion includes several PHD domains of NSD1, which have previously been suggested to be important for leukemogenesis (PMID: 17589499). The discussion section has been modified to add:

We envision that a similar mechanism targets other NUP98 fusions containing H3K4me3-recognizing reader domains (e.g., NUP98::PHF23) to leukemogenic loci, complementing direct targeting of the HOX genes through DNA sequence recognition in fusions containing DNA-binding domains (e.g., NUP98::HOXA9).

Reviewer #2 (Public review):

In this manuscript, the authors investigate how the oncogenic fusion protein NUP98KDM5Aalters gene expression in leukemia, using a combination of cellular experiments with model and patient cell lines, as well as in vitro studies. Upon transfection of U2OS cells with mEGFP-tagged NUP98-KDM5A, the authors show that the fusion proteins form sub-micrometre puncta, whereas KDM5A alone does not. These foci are also observed at expected native expression levels (using OpenCell data). The tag has an effect here, as switching to an mCherry tag raises the apparent saturation concentration for phase separation. Finally, the authors show via super-resolution imaging that the foci correlate with H3K4me3 distribution.

In vitro, the fusion protein forms amorphous, gel-like condensates at double-digit nanomolar concentrations. Truncation analysis identifies PHD3 of KDM5A as required for maximal phase separation, consistent with the ability of the protein to bind H3K4me3 peptides. Addition of polynucleosomes increases the amount of fusion protein partitioning into the condensate in anH3K4me3-binding-dependent manner. Condensates are gel-like with slow internal dynamics in vitro; in cells, however, the dynamics depend on the position of the EGFP tag (no corresponding experiments with mCherry are shown). Reconstitution with H3K4me3- and H3K4me0-modifiedarrays shows colocalization with both wild-type NUP98-KDM5A and the binding mutant. Here, H3K4me3 arrays recruit ~20% more protein and yield gel-like structures in a manner dependent on the PTM and on the PHD finger.

In cells, the fusion protein colocalizes with H3K4me3-marked loci, including the HOX clusters, as confirmed by FISH. Finally, re-analysis of published expression datasets from patient cells shows that genes are predominantly upregulated and that the upregulated genes are H3K4me3-marked.

This is a well-executed mechanistic study. The data convincingly establish that NUP98KDM5A forms sub-micrometre foci at realistic expression levels, that these foci correlate with H3K4me3-marked sites, that the PHD3-H3K4me3 interaction mediates chromatin binding while the NUP98moiety drives phase separation in vitro, that foci in cells overlap genes heavily decorated with H3K4me3, and that H3K4me3-marked genes are those found to be upregulated in patient datasets. These are important mechanistic findings and of interest to the community.

Still, the functional/causal link is a bit more tentative, as the data is mostly correlative, since it is not directly established that there is feedback between H3K4 methylation, NUP98KDM5Arecruitment, phase separation and target gene overexpression. An experiment that could further bolster this claim would be a direct test of whether NUP98-KDM5A expression drives overexpression of bound genes, e.g. expression of the fusion protein vs PHD- and NUP98-mutant variants, followed by qPCR of target genes, such as the HOX cluster, and possibly H3K4me3 ChIP at the same loci. As all the constructs and cell lines exist, this could be feasible and would substantially strengthen the manuscript.

We thank the reviewer for the thoughtful evaluation and agree that the causal link betweenH3K4me3 recognition, condensate formation, and gene activation remains partly correlative. Experiments such as qPCR or ChIP following expression of WT versus mutant constructs would indeed strengthen the causal chain. However, performing these assays across multiple constructs and loci in a physiologically relevant system is not feasible within the current revision cycle. We have added text acknowledging this limitation and clarifying that our study focuses on establishing the biophysical mechanism of targeting, while functional consequences are inferred from patient datasets rather than new perturbation experiments.

We modified the Study limitations section of the Discussion to add:

Similarly, our study focuses on the biophysical mechanism of chromatin targeting by the NUP98::KDM5A oncofusion, with functional consequences inferred from patient-derived datasets rather than defined perturbation experiments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 1 - Figure Supplement 2: show co-localisation of large droplets of the chromatin-binding mutant with nucleoli by co-immunostainings, using nucleolar markers.

(2) Figure 1E: Show another histone mark as a control, ideally H3K27me3.

(3) The authors are encouraged to stick to the recommended nomenclature of fusion genes(https://www.nature.com/articles/s41375-021-01458-0).

Reviewer #2 (Recommendations for the authors):

(1) The phase-separation behaviour clearly depends on the fusion FP, as the switch from mEGFP to mCherry shifts the apparent saturation concentration to ~200 nM. The authors should discuss, and where possible test, how much of the observed behaviour is attributable to the FP itself: what happens in the absence of any FP, and which construct (mCherry- or mEGFP-tagged) the authors consider the better proxy for the untagged fusion protein.

(2) This is particularly relevant given that the in-cell dynamics (FRAP) are reported to depend on the position of the EGFP tag, and no corresponding mCherry experiments are shown.

(3) The authors claim a patient NUP98-KDM5A concentration of ~180 nM. This is based on data for NUP98 in HEK293 cells, with the added correction factor for having only one allele mutated in patients. Still, the direct jump from HEK293 to patient leukemia cells is big; so the authors should formulate this more carefully: no conc. determination was done directly in patients.

(4) Chicken erythrocyte chromatin: What is the endogenous H3K4me3 level in the chicken erythrocyte chromatin used here?

(5) Figure 1 - Figure Supplement 3B. The legend defines the square as the mean but does not explain the remaining symbols (vertical lines, horizontal lines, grey versus black dots). Please define these plot elements.

(6) In the reconstitution experiments, the arrays and the condensates appear to colocalize only weakly, and, a bit counterintuitively, the strongest apparent colocalization is seen for the NUP98KDM5A binding mutant. Can the colocalization be quantified and interpreted?

(7) Figure 2 - Figure Supplement 3. Raising the chromatin concentration from 12.5 to 100 nM produces little visible change in the images. Where does the additional chromatin go? Does it stay in solution? As in point 4, the best colocalization again appears to be obtained with the mutant, which is unexpected and a bit difficult to reconcile with the proposed H3K4me3-PHDdrivenrecruitment model.

(8) That highly expressed genes in patients carry H3K4me3 is basically expected and is not by itself informative. The relevant question is the origin of the effect: is H3K4me3, and the associated upregulation, a consequence of NUP98-KDM5A condensate formation? Analyzing the direct effects of NUP98-KDM5A (and mutants) on specific target gene expression profiles could help to dissect this further.

We thank the reviewers for these recommendations. We have made the following revisions to the manuscript:

We replaced NUP98-KDM5A with NUP98::KDM5A, in accordance with the recommended nomenclature. We made this change in both the text and the figures. We also corrected other NUP98 on confusions to reflect this recommendation.

We have revised Figure 1 – Figure Supplement 3B and the accompanying legend to describe the symbols used in this figure.

Author response:

I am writing to provide a description of our planned revisions. We thank the reviewers for their thoughtful comments on the manuscript. All three reviewers had the primary concern of “lack of saline-treated control.” We had, in fact, included saline-treated control in our design, and shown some of this data in the original submission (Supplemental data Fig 1G). We agree with the Editor’s note that more analysis for saline sessions should be provided. The planned revisions will include additional saline data to compare saline injections on behavior (as shown for psilocybin on figure 1), on reward-preferring and non-preferring cluster analysis (as shown for psilocybin on figure 3), and on action decoding and encoding (as shown for psilocybin on figure 6).

It should be emphasized that the work involved outbred rats performing a complex probability-shifting decision-making task while freely moving in an operant box. Some of the comments by reviewer 1 (such as considering long/changing latencies to retrieve reward as “extraordinarily” or “abnormally” long) suggest that there may have been a mix-up with what is common in freely-moving rats versus simpler and head-fixed mouse paradigms. This distinction is relevant to some of the concerns raised by reviewer 1. First, our n is well within the range seen in electrophysiological studies in behaving rats as most these studies utilize n=5-9 (e.g., Sias et al., Nature Neuro, 2024; Maor et al., Nature Comm, 2026). Second, our analysis dealt with shifting latencies accordingly (e.g. time-locking to action) and focused on within subject performance because in complex cognitive tasks such as ours, there is a considerable amount of baseline performance variability in outbred rats. It is, therefore, common, and clinically relevant, to focus on within subject analysis of drug or vehicle effects. This has been the case with previous studies on the effect of psilocybin on cognitive flexibility (e.g. Torrado Pacheco et al, NPP 2023) and was our approach here. The additional saline data will hopefully convince the reviewers and interested readers that the reported effects of psilocybin were not an artifact of i.p. injections

Author response:

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

eLife Assessment:

This study provides valuable insights into humans' ability to generalize knowledge of learned graph structures to new experiences that share the same structure but are built from different stimuli. However, the evidence for the authors' claims is incomplete, with the main claims of structural generalization and compositionality only partially supported by MEG and behavioral data. This study will be of interest to cognitive neuroscientists studying structure learning and generalization.

We thank the editor and reviewers for a positive evaluation of our work and constructive suggestions to improve our manuscript.

The reviewers' comments motivated textual modifications to the manuscript, changes and additions to figures and conduct of further analyses.

We believe that the changes made in response to the reviewers' comments and suggestions provide for a substantially improved revised manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary of the paper:

The paper presents an elegant task designed to investigate humans' ability to generalize knowledge of learned graph structures to new experiences that share the same structure but are built from different stimuli. Using behavior and MEG recordings, the authors test evidence for neural representation and application of structural knowledge.

We appreciate this overall positive evaluation of our work and suggestions to strengthen the empirical support for the claims made in the paper.

(1) While the task design is elegant, it isn't clear to me that the data support all the claims made in the paper. I have detailed my concerns below.

The authors claim that their findings reveal "striking learning and generalization abilities based on factorization of complex experiences into underlying structural elements, parsing these into distinct sub processes derived from past experience, and forming a representation of the dynamical roles these features play within distinct subprocesses." And "neural dynamics that support compositional generalisation, consistent with a structural scaffolding mechanism that facilitates efficient adaption within new contexts".

(a) First, terms used in these example quotes (but also throughout the paper) do not seem to be well supported by data or the task design. For example, terms such as 'compositional generalisation' and 'building blocks' have important relevance in other papers by (some of) the same authors (e.g., Schwartenbeck et al., 2023), but in the context of this experiment, what is 'composition'?

We agree that our use of composition is less technical and formal than the nested and recursive forms of composition using “building blocks” reported in previous work (e.g., Schwartenbeck et al., 2023). In this experiment we study composition of smaller graphs via superimposition of their outputs. The superimposed “compound” outputs can be viewed as outputs of a single, more complex, graph. This is a special case of all possible ways that graphs can be composed from other graphs, and does not depend on a complex syntax for their combination (although more complex combination rules, other than multiplication are theoretically possible). Nevertheless, in accordance with common definitions of compositionality, this leads to a generative setup, given that a huge number of graphs can be expressed as the product of smaller graphs in this way.

Figure panel (Fig 1A) illustrates this precise point. Importantly, we argue this kind of composition is ubiquitous in real-world learning scenarios where multiple independent processes contribute to the holistic experience of a situation.

Based on the reviewer’s suggestion we have now amended the manuscript introduction to render the distinction between different definitions, and usage, of the term composition more salient.

It is our understanding that this form of flexible, combinatorial, reuse of factorized prior knowledge is considered a specific instance of composition. Indeed, this understanding is supported by a cognitive-computational neuroscience literature that adheres to similar conceptualizations of compositionality, e.g., Barron et al., 2013 Nat Neuro; Rubino et al., 2023 PsyArxiv; Luettgau et al., 2024 PNAS.

We add a paragraph to the introduction section elaborating on what we mean by graph factorization and its relevance for questions of compositional generalization (reproduced below for convenience).

To address these questions, we developed a sequence learning paradigm based on a graph theoretical concept of graph factorization, emulating environments whose dynamics are the product of multiple simultaneous subprocesses. “Product graphs (Cartesian product), wherein the joint dynamics of two or more graph factors create complex product state space dynamics that can be factorized (and simplified) into constitutive factors, provides a compelling and flexible test bed for probing compositional generalization of multiple (independent) and simultaneously unfolding subprocesses.” Examples of such graph products and their factorizations, from a vast space of possible combinations, are provided in Figure 1A. Here we take inspiration from prior studies in neuroscience (e.g., Barron et al., 2013; Rubino et al., 2023; Schwartenbeck et al., 2023) and a prior cognitive literature, e.g., recursive operations over hierarchies (O’Donnell et al., 2009, 2011), hierarchical function composition, or rich forms of semantic composition in language to create complex concepts (Murphy, 1988).

(2) Can the authors demonstrate clear behavioural or neural evidence for compositional use of multiple graph structures, or alternatively remove reference to these terms? In the current paper, it seems to me that the authors are investigating abstract knowledge for singular graph structures (together with the influence of prior learning), as opposed to knowledge for the compound, more complex graph formed from the product of two simpler graphs.

We thank the reviewer for this important clarification, and agree our language should more precisely distinguish what the task design requires from what our data directly demonstrate. The reviewer is correct that our analyses primarily provide evidence for the abstraction and transfer of a single previously-experienced graph structure to novel stimuli, rather than direct evidence that participants combine two independently learned structures into a novel compound representation. We agree this distinction is important, and we have revised our language throughout the manuscript accordingly, reserving "compositional generalization" to describe the broader task structure (in which every compound stimulus is the joint product of two simultaneously evolving subprocesses, and the specific compound experienced during transfer learning was never observed during prior learning) and using more precise language: "decomposition," "abstraction," and "transfer" of single structural components to describe what our behavioral and neural evidence actually establishes. We have not claimed direct evidence that participants compositionally construct novel joint representations from two previously separate structures; rather, our evidence concerns the selective reuse of one such component when it recurs across learning phases, embedded in a novel pairing with another, entirely new structural component. We have adjusted the manuscript throughout and changed the title of the paper to “A neural mechanism for compositional structure transfer in humans”, to more adequately reflect the evidence presented.

(3) While I would like to be convinced that this data provides evidence for the transfer of abstract, structural knowledge, I think the authors either need to provide more convincing evidence or tone down their claims.

Can the increase in neural similarity between stimuli mapping to the same abstract structural sub-process not be explained by temporal proximity in experiencing the transitions (e.g., Cai et al., 2016)? Indeed, behavior seems to be dominated by direct experience of the structure as opposed to applying abstract knowledge of equivalent structures (and, as a result, there is little difference in behavioural performance between experience and inference probes).

The reviewer makes an astute observation while providing a constructive challenge. We agree that distinguishing transfer of abstract structural knowledge from effects driven by direct temporal experience is critical, and we appreciate this opportunity to clarify our reasoning on this point.

The reviewer suggests that increased neural similarity between stimuli that map to the same abstract structural sub-process might be explained by a temporal proximity in experience, as shown in prior work (e.g., Cai et al., 2016). We agree that temporal proximity is a potentially powerful determinant of representational similarity. Likewise, we do not dispute that temporal statistics of experience play an important role in shaping such neural representations. Nevertheless, we believe these accounts do not provide a sufficient explanation for our results, which we consider reflects a consequence of being exposed to the outputs produced by sequences drawn from an underlying graph structure and a prior learning of these sequences.

In our task, the temporal statistics of stimulus experience are fully dictated by the transition structure of the graph. Different graph structures necessarily impose different constraints on temporal proximity (e.g., how many steps it takes to revisit a given node, which nodes are encountered at similar temporal distances, etc.). Thus, if stimuli that occupy equivalent structural roles across different graphs come to be represented more similarly, this is precisely because learners have abstracted over the specific transition structure that governs these temporal relationships. In other words, consistent with our previous computational findings that models based on temporal difference learning mechanisms account well for behavioural response patterns (Luettgau et al., 2024 PNAS), temporal proximity is not a confound but instead is a likely mechanism through which structural knowledge is acquired. Critically, our key claims concern transfer across learning contexts, and not sensitivity to temporal proximity within a single experience stream. By design, the selective learning improvements observed in each group during transfer cannot be explained by temporal proximity alone, because the relevant temporal statistics in the transfer phase are novel and differ across groups. The fact that prior learning selectively facilitates subsequent learning depending on an earlier experience of an abstract structure indicates participants are not simply tracking local temporal regularities, but instead are reusing previously learned structural knowledge to guide learning within a new context.

We agree that behavior in our task is strongly influenced by direct experience, and we do not claim that participants rely exclusively on abstract structural knowledge. Indeed, the relatively small differences between experience and inference probes are consistent with the view that abstraction complements and facilitates, rather than replaces, learning from direct experience. Our claims are therefore deliberately modest: we argue for the transfer of abstract structural knowledge that shapes learning dynamics and neural representations, not for behavior dominated by explicit inference over abstract graphs.

To avoid any criticism related to over-interpretation, we have toned down our language and clarify throughout introduction, results and discussion section of the manuscript that (i) temporal proximity is an intrinsic feature of graph structure, (ii) neural effects reflect (in part) abstraction over these structured temporal relationships, and (iii) that our results provide evidence for transfer of structural knowledge that biases learning, rather than for fully context-independent representations or strong behavioral generalization.

(4) The strongest evidence for neural representation of abstract task structures seems to be the increase in similarity by transition type. But this common code for 'transition type' is only observed for 6-bridge graphs and only for experienced transitions. There was no significant effect in inference probes. Therefore, there doesn't seem to be evidence for the application of a knowledge scaffold to facilitate transfer learning. Instead, the data reflects learning from direct experience and not generalisation.

We appreciate the reviewer's point, and agree it deserves a careful investigation. We carefully considered how this correlation could be interpreted under a non-transfer, pure direct-experience account. Our interpretation is that even if all graph learning relies entirely on direct experience, a correlation is still expected due to individual differences in learning ability. Under this framework, higher-ability participants are simply more likely to directly discover the same structural component (the 6-bridge) across both sessions (prior and transfer learning), which in turn supports higher MEG transition decodability. Concurrently, these same participants will exhibit higher behavioral accuracy due to their superior learning capacity. Importantly, under this account, these higher-ability participants should also show higher behavioural accuracy during the transfer phase for the 4-cycle component, predicting (a) a positive correlation between our transition decoding signal and 4-cycle behavioural accuracy, and (b) a positive correlation between 4-cycle and 6-bridge behavioural accuracy themselves, within each prior learning group.

We tested both predictions directly. For (a), in the 6-bridge prior group, average decoding strength at timepoints showing a selective significant group difference correlated with experience probe performance on the 6-bridge graph during transfer learning (ρ = .48, p = .016, surviving correction for two comparisons, α = .025), but the corresponding correlation with 4-cycle behavioural accuracy did not reach significance (ρ = .38, p = .071). We acknowledge, however, that a direct comparison of these two dependent correlations (Steiger's test) did not reach significance (p = .66).

For (b), we directly correlated 4-cycle and 6-bridge transfer accuracy within each prior learning group. For experience probes, this correlation was significant in the 4-cycle prior group (ρ = .51, p = .010) but not in the 6-bridge prior group (ρ = .24, p = .257); for inference probes, the pattern reversed, with a significant correlation in the 6-bridge prior group (ρ = .42, p = .035) but not the 4-cycle prior group (ρ = .16, p = .452). In neither probe type did a direct comparison of the two groups' correlation coefficients reach significance (experience probes: Z = -1.06, p = .291; inference probes: Z = .95, p = .340). Given that two of these four single-group correlations were nominally significant (without correction for multiple comparisons) while the corresponding between-group comparisons were not, and given the inconsistency in which group/probe-type combination shows the effect, we consider this pattern inconclusive rather than supportive of a clear general-ability signal linking performance on the two graph components.

We therefore cannot statistically rule out the general-ability account with the current sample, and have revised our interpretation accordingly: rather than claiming strict specificity to the 6-bridge structure, we now describe the correlation as selective to 6-bridge experience probes in this sample, while acknowledging that distinguishing structural reuse from a more general learning ability to represent novel relational structure remains an open question. We have added the decoding-strength comparison as a new Supplementary Figure 5, showing decoding-strength correlations with both 4-state and 6-bridge graph performance side by side, and report the direct behavioural correlation between graph components in the text, and have revised the relevant main-text passage to match these updated values.

We also wish to address why this correlation was selective to experience probes and did not extend to inference probes. We agree that, under an assumption of perfectly learned and context-independent abstract representations, one might expect performance on experience and inference probes to relate equally to the decoding signal. We believe the reviewer's concern is valid only under an assumption of perfect abstraction. In our task, abstract roles correspond to latent structural variables that are learned gradually and with uncertainty. Under such conditions, role inference is inherently context-dependent: the role of a given stimulus is not inferred in isolation, but in relation to the compound within which it appears. For example, if one element of a compound is already known with high confidence to belong to a particular subgraph, the role of the second element can be inferred more reliably; in contrast, when both elements are themselves uncertain, role inference becomes less precise. Critically, learning is unlikely to be uniform across compounds, as structural knowledge may be acquired with variable precision for different stimulus pairings depending on their frequency, co-occurrence statistics, and position within a sequence. This variability in learning precision means we would expect corresponding variability in a participant's ability to infer dynamical roles across different compound types, and consequently in their ability to make accurate predictions about those compounds. Under this account, our MEG signal, which indexes role-based representational structure specifically for experienced compounds, most directly reflects knowledge precision for those items; a correlation with inference probe accuracy requires an additional inferential step from experienced to novel compounds, introducing noise proportional to uncertainty in the underlying learned representations. We have revised the Discussion to make this reasoning more explicit.

(5) The authors frequently suggest that they are providing insight into temporal dynamics, but there is no mention of particular oscillations or particular temporal sequences of neural representation that support task performance.

We thank the reviewer for highlighting this. We agree our use of the term "temporal dynamics" is potentially misleading, and we have now revised the manuscript accordingly. Our analyses did set out to identify specific neural oscillations, rhythmic processes, or temporally ordered stages of computation that support task performance. Rather, time-resolved MEG analyses is a method that allows us to track when representational content is expressed during stimulus processing, serving three research questions about subprocess-specific representational similarity, dynamical role representations, and relationship to behavioral transfer performance; as opposed to characterizing the temporal organization of underlying computations per se.

We have now removed or replaced references to "temporal dynamics" and "neural dynamics" throughout the manuscript where these might be interpreted as claims about oscillatory or sequentially structured neural mechanisms. Instead, we now frame our conclusions in terms of representational content and its modulation by prior learning experience. We believe this aligns our language with what the data actually support and removes potential confusion regarding the scope of our claims.

(6) Regardless of point (b), can the authors provide more convincing evidence for a graph structure being represented per se (regardless of whether this representation is directly experienced or inferred)? From Figure 3C, it seems that the model RDM doesn't account for relative distance within the graph. Do they see evidence for distance coding? Can they reconstruct the graph from representational patterns using MDS?

We thank the reviewer for raising this point. The reviewer is correct that the model RDM shown in (previous) Figure 3C does not specifically capture relative distance within the graph and asks whether there is evidence for distance coding or whether the graph can be reconstructed using techniques such as MDS. We agree that distance-based representations are one possible signature of graph knowledge, with such effects reported in a prior literature. However, our theoretical focus is on an investigation of a more functionally relevant aspect of graph structure learning and reuse of abstracted knowledge: the representation of graph nodes according to their structural roles or positions within a graph.

To address the question more directly, we ran an additional sensor-level RSA analysis using the localizer task data, comparing representational changes from PRE to POST learning. Specifically, we examined whether stimuli in the 6-bridge graph that map onto the same structural roles (e.g., boundary, intermediate, central) within the relevant graph structures show greater neural similarity from before to after learning, and whether this effect depends on the graph structure experienced during prior learning. This new analysis revealed a cluster-based, permutation-corrected, interaction effect between prior learning group and graph factor, consistent with a representational similarity increase selectively for stimuli sharing the same structural role in a graph structure relevant to each group’s prior experience. Importantly, this effect occurs at similar time points as our earlier RSA effects based on overall stimulus-set similarity, suggesting that both analyses capture related aspects of the same underlying representational processes.

We believe this role-based representational similarity provides more direct evidence for graph-structured representations and their transfer across learning than distance-based or MDS reconstructions in our task context. First, distance within the graph is necessarily correlated with temporal proximity of experience, making it difficult to disentangle distance coding from local transition statistics. Second, multiple distinct graph structures used in our experiment (e.g., cycles, lines, and bridges) share overlapping distance relationships but differ in their higher-order structural roles. Our analysis therefore targets those aspects of structure that are invariant across surface features and that are most relevant for transfer across learning contexts.

For these reasons, while we do not claim we can reconstruct full graph geometry from neural patterns, our results are consistent with an organization of neural representations according to abstract structural positions within a graph, that is independent of specific stimulus identities. We have added a new panel to Figure 3 illustrating this role-based RSA effect and also expanded the Methods and Results sections to describe this analysis in detail. We believe this addition provides more convincing evidence that participants represent graph structure at an abstract level, even when that structure is not explicitly experienced in the same form during the localiser task. We thank the reviewer for encouraging this more specific analysis, as it significantly strengthens our claims.

“To test whether localiser representations of abstract graph structure generalised across sets experienced in the main task, we performed RSA separately for PRE and POST localisers. Structural roles were derived from each participant’s learning-phase transition sequences. For 4-state graphs, nodes were assigned to two matched role bins (boundary-like vs central-like) based on first-encounter order within each phase. For 6-state graphs, roles were determined either from node degree (6-line: boundary, intermediate, central). For 6-bridge graphs we used a predefined structural template. Specifically, the first eight valid transitions in the learning phase were mapped onto a fixed sequence of structural roles (central–intermediate–boundary–central–central–intermediate–boundary–central). Each node was assigned a role based on the majority role it occupied across its occurrences in these eight steps (ties resolved in favour of central > intermediate > boundary). For the localiser data, at each time point and sensor we estimated condition-specific activations using a GLM with 20 dummy-coded regressors (10 identities × 2 sets). This yielded sensor-wise beta patterns for each condition. Cross-set representational dissimilarities were computed using an L1 distance metric (mean absolute difference across sensors), resulting in 4×4 and 6×6 cross-set RDMs at each time point. We then summarised each RDM according to structural role: within-role distances (same role across sets), between-role distances (different roles), and their difference (delta = between − within). To control for unequal pair counts, between-role comparisons were subsampled to match the number of within-role pairs (200 repetitions). This produced time-resolved structural generalisation indices for 4-state and 6-state graphs, which were submitted to group-level statistical analyses as described above.”

(7) In general, the figures are not very clear, and the outcome from statistical tests is not graphically shown. The paper would be easier to digest if, for example, Figures 1-2 were made clearer and statistical significance relative to chance were indicated throughout. To give two examples: (i) Figure 1 should clearly indicate what is meant by observed and held-out transitions and whether it is just the transition or also the compound that is new to the participant. (ii) Figure 2D-E could be shown with relevant comparisons and simpler statistical comparisons. Currently, it is hard to follow without carefully reading the legend.

We have taken the reviewer’s point on board and have revised the figures to improve clarity. Specifically, we have improved labeling and visual annotation in Figure 1 to clearly distinguish observed versus held-out transitions and to highlight the key experimental manipulations. We have also simplified the presentation of behavioral results in Figure 2D–E and made the most relevant statistical comparisons more explicit, with statistical outcomes now indicated directly in the figures where appropriate.

We believe these changes improve readability and reduce the burden on the reader, while still relying on the figure captions to convey essential methodological details and interpretation, following standard practice. See Figure 1 and Figure 2.

Reviewer #1 (Recommendations for the authors):

(1) For the classifier: what was the overall accuracy of the classifier when tested on held-out examples of the same stimuli? Relative to chance? Relative to entirely different stimuli that have the same transition type (e.g., line 424)?

(2) In the Results paragraph 2 can you state how many subjects had prior exposure to 4-state vs how many had prior exposure to 6-state?

This has now been added these data to the results section, reproduced below for convenience:

In brief, participants “(N = 50, N = 25 subjects per condition)” performed a sequence learning task, observing image sequences produced by walks on product graphs constructed from smaller graph factors (Fig. 1A and B).

Reviewer #2 (Public review):

Summary:

The authors aimed to investigate the temporal dynamics of how prior experiences shape learning in new complex environments by examining whether the brain reuses abstract structural components from those experiences. They employed a sequence learning task based on graph factorization and recorded neural activity using magnetoencephalography (MEG) to investigate how the underlying graph factors are reused to support learning and inference in a new graph. MEG data was derived from passive stimulus presentation trials, and behavior was assessed through a small number of probe trials testing either experienced or inferred successions in the graph. Representational similarity analysis of the MEG data was performed at a quite aggregated level (the principal components explaining 80% of the variance). The authors report (1) enhanced neural similarity among stimuli that belong to the same graph-factor as well as (2) a correlation between abstract role representations, corresponding to particular positions in the graph, and performance in experience-probes but not in inference-probes.

Overall, the findings are congruent with prior research on neural correlates of structural abstraction. They offer an elegant, well-suited task design to study compositional representations, replicating the authors' earlier finding and providing temporal information on structural generalisation in a sequence learning task.

We thank the reviewer for this positive evaluation of our work and insightful comments and suggestions.

(1) The first finding is considered evidence for representational alignment of the graph factors. However, alignment seems to be just one possible arrangement underlying the increased similarity between stimuli of the same vs different graph factors. For instance, a simple categorical grouping of stimuli belonging to the same graph, rather than their structural alignment, could also underlie the reported effect. The wording should be adjusted to avoid over interpretation.

We agree with the reviewer that increased neural similarity between stimuli associated with the same graph factor does not uniquely imply representational alignment in its strongest sense, and could in principle also reflect a more general categorical grouping of stimuli based solely on belonging to the same graph. We revised the manuscript to tone down the wording and avoid overinterpretation, replacing references to “representational alignment” with more neutral language that refers to increased within-factor representational similarity.

At the same time, we believe that additional analyses introduced in the revised manuscript constrain alternative accounts. In particular, our new analysis on localiser data, examining representational changes from PRE to POST learning for stimuli that map onto the same structural roles within relevant sub-process graph structures. This analysis showed the presence of a cluster-based, permutation-corrected, interaction effect between group and graph factor, indicating that representational similarity increases selectively for stimuli sharing the same structural role, rather than simply increased similarity for all stimuli associated with the same graph.

Because these role-based groupings cut across specific stimulus identities and cannot be reduced to a single categorical label for an entire graph, we believe this result provides specific evidence that neural representations are shaped by internal structural properties of the graph, rather than reflecting the emergence of a coarse categorical distinction between graph types. We have added this analysis as a new panel to Figure 3 and expanded the Results and Methods sections accordingly (reproduced below for convenience):

“The observed increase in neural similarity between stimuli associated with the same graph factor could, in principle, reflect a more general categorical grouping of stimuli belonging to the same graph factor, rather than reflecting an abstract graph representation. To address this alternative account, we examined whether neural similarity in the localizer task is specifically structured according to the graph-theoretic role each stimulus occupies within its graph, using a finer-grained theoretical RDM that distinguishes between boundary, intermediate, and central positions. Structural roles were derived from each participant's learning task sequences and defined by graph topology. For Component 6, roles were assigned using a bridge-graph traversal template (for Condition 6, whose prior learning involved the bridge graph) or degree-based assignment (for Condition 4, whose prior learning involved a line graph): boundary nodes were defined as nodes with degree 1 (graph periphery); intermediate nodes as neighbours of boundary nodes; and central nodes as the remaining, more densely connected nodes. For Component 4, two roles were distinguished, boundary-like nodes (those encountered first and last in the sequence traversal) and central-like nodes (those encountered second and third), reflecting structural position within the graph rather than arbitrary temporal sequence. For further details of role assignment, see Methods. This analysis revealed a cluster-based permutation-corrected interaction (P_FEW < 0.05, non-parametric permutation test, Figure 3E) between prior learning group and graph factor at overlapping time windows with the previously reported PCA and sensor-level analyses investigating feature-mappings to abstract graph factors. We did not observe significant and multiple comparisons corrected prior learning group and graph factor main effects (all P_FEW > 0.90, non-parametric permutation test). These results indicate that representational similarity increased selectively for stimuli sharing the same structural role in the graph structure relevant to each group’s prior experience. Critically, this effect was not observed uniformly for all stimuli associated with the same graph, arguing against a purely categorical grouping explanation. Instead, these findings provide evidence that learning induces representations that reflect higher-order relational structure, capturing graph-theoretic roles that are invariant across surface features of the embedding stimuli and support transfer across learning contexts.

Taken together, our findings indicate a task-induced, learning-related increase in neural similarity for stimuli sharing a structural role in subprocesses common across task phases and is compatible with a structural scaffolding mechanism, though we do not claim these representations are fully context-independent.

“To test whether localizer representations of abstract graph structure generalised across sets experienced in the main task, we performed RSA separately for PRE and POST localisers. Structural roles were derived from each participant’s learning-phase transition sequences. For 4-state graphs, nodes were assigned to two matched role bins (boundary-like vs central-like) based on first-encounter order within each phase. For 6-state graphs, roles were determined either from node degree (6-line: boundary, intermediate, central). For 6-bridge graphs we used a predefined structural template. Specifically, the first eight valid transitions in the learning phase were mapped onto a fixed sequence of structural roles (central–intermediate–boundary–central–central–intermediate–boundary–central). Each node was assigned a role based on the majority role it occupied across its occurrences in these eight steps (ties resolved in favour of central > intermediate > boundary). For the localiser data, at each time point and sensor we estimated condition-specific activations using a GLM with 20 dummy-coded regressors (10 identities × 2 sets). This yielded sensor-wise beta patterns for each condition. Cross-set representational dissimilarities were computed using an L1 distance metric (mean absolute difference across sensors), resulting in 4×4 and 6×6 cross-set RDMs at each time point. We then summarised each RDM according to structural role: within-role distances (same role across sets), between-role distances (different roles), and their difference (delta = between − within). To control for unequal pair counts, between-role comparisons were subsampled to match the number of within-role pairs (200 repetitions). This produced time-resolved structural generalisation indices for 4-state and 6-state graphs, which were submitted to group-level statistical analyses as described above.”

(2) The second finding of abstract role representations is indeed expected for structural generalisation. While the data presents an interesting indication, its interpretability is constrained by a lack of testing for generalization of the effect to other graph structures (e.g., to rule out graph-specific strategies) as well as the absence of a link to transfer performance in inference-probes. The authors argue that the experienced transitions the classifier was trained on might be more similar in process to the experience-probes than the inference-probes. However, as inference-probes are the key measure of transfer, one could argue that if abstract role representations truly underlie transfer learning, they should be evident in the common neural signal.

The reviewer provides a thoughtful comment and we agree that, under an assumption of perfectly learned and context-independent abstract representations, one might expect this would be related equally to performance in experience and inference probes. Below, we clarify the scope of our claims, including presenting additional neural evidence for abstract role representations, and argue that an absence of a strong neural-behavioral correlation for inference probes is not inconsistent with our proposed abstract structural knowledge account of transfer learning.

First, we acknowledge that our experiment tests generalization only across two graph families, rather than across a broader set of graph structures. While we think it unlikely that our findings are idiosyncratic to cycles or bridge-like graphs, a we now limit our claims and emphasise a future need for testing generalization across additional graph families (see discussion section as reproduced below)

“We concede that the present experiment examines generalization across two families of graph structures, rather than across a broader space of possible graphs. While we consider it unlikely that our findings are idiosyncratic to cycles, lines and bridge-like graphs, we acknowledge that further work will be needed to support abstraction beyond the limited graph structures studied here.”

Second, to provide more direct neural evidence that abstract structural roles within the studied graphs are represented per se, we add a new analysis that uses independent localizer task data. In this analysis, we performed a sensor-level RSA contrasting pre- and post-learning representations. Specifically, we test whether stimuli that occupied the same role within learned graph substructures became more neurally similar after learning. This localizer RSA revealed a cluster-corrected interaction effect between prior learning group and graph factor, expressed in an increased representational similarity for stimuli mapping onto equivalent structural roles, independent of specific stimulus identities and outside the task context of the main learning phase. This result supports the proposal that participants form abstract, role-based, representations of graph structure where these representations are not tied to a particular transition sequence or probe type. This finding adds an important insight in that it goes beyond establishing role representations for the 6-bridge graph factor, enabling us to make claims about generalization of structural knowledge of the 4-cycle graph factor in the 4-cycle prior condition (thereby to some extent showing a wider generalization across more structural forms).

“To test whether localizer representations of abstract graph structure generalised across sets experienced in the main task, we performed RSA separately for PRE and POST localisers. Structural roles were derived from each participant’s learning-phase transition sequences. For 4-state graphs, nodes were assigned to two matched role bins (boundary-like vs central-like) based on first-encounter order within each phase. For 6-state graphs, roles were determined either from node degree (6-line: boundary, intermediate, central). For 6-bridge graphs we used a predefined structural template. Specifically, the first eight valid transitions in the learning phase were mapped onto a fixed sequence of structural roles (central–intermediate–boundary–central–central–intermediate–boundary–central). Each node was assigned a role based on the majority role it occupied across its occurrences in these eight steps (ties resolved in favour of central > intermediate > boundary). For the localiser data, at each time point and sensor we estimated condition-specific activations using a GLM with 20 dummy-coded regressors (10 identities × 2 sets). This yielded sensor-wise beta patterns for each condition. Cross-set representational dissimilarities were computed using an L1 distance metric (mean absolute difference across sensors), resulting in 4×4 and 6×6 cross-set RDMs at each time point. We then summarised each RDM according to structural role: within-role distances (same role across sets), between-role distances (different roles), and their difference (delta = between − within). To control for unequal pair counts, between-role comparisons were subsampled to match the number of within-role pairs (200 repetitions). This produced time-resolved structural generalisation indices for 4-state and 6-state graphs, which were submitted to group-level statistical analyses as described above.”

Third, in relation to the relationship between neural role representations and transfer performance during inference probes, we believe the reviewer's concern is valid only under an assumption of perfect abstraction. In our task, abstract roles correspond to latent structural variables that are learned gradually, and with uncertainty. Under such conditions, role inference is inherently context-dependent: the role of a given stimulus is not inferred in isolation, but in relation to the compound within which it appears. For example, if one element of a compound is already known with high confidence to belong to a particular subgraph, the role of the second element can be inferred more reliably. In contrast, when both elements are themselves uncertain, role inference becomes less precise. Critically, learning is unlikely to be uniform across compounds, as structural knowledge may be acquired with variable precision for different stimulus pairings depending on their frequency, co-occurrence statistics, and position within a sequence. This variability in learning precision means we would expect corresponding variability in a participant's ability to infer dynamical roles across different compound types, and consequently in their ability to make accurate predictions about those compounds.

Our MEG signal indexes role-based representational structure specifically for experienced compounds, and most directly reflects the precision of structural knowledge for those items. Therefore a correlation between a MEG signal and accuracy on inference probes is expected to be weaker, since it requires an additional inferential step from experienced to novel compounds, a step that is likely to introduce additional noise proportional to the uncertainty in the learned representations. Ideally we would expect such a correlation to be present for inference probes as well, since better structural knowledge about experienced compounds should in principle support better generalisation to novel ones. However, we consider we are insufficiently powered to detect this weaker relationship and interpret an absence of a significant correlation for inference probes as not inconsistent with a structural scaffolding account.

Finally, we emphasize that the absence of a strong correlation between aggregate neural decoding measures and aggregate inference-probe performance should not be taken as evidence against abstract learning. Inference performance is likely to be supported by multiple sources of information (including partial structural knowledge and heuristic strategies), whereas neural decoding captures the stability of representational geometry at a population level. The newly added localizer RSA results demonstrate that abstract role representations are present in the neural signal, while at the same time their task-dependent expression may not always be directly mirrored at the level of inference-probe behavior.

We have an added a paragraph caveating our findings to the discussion section (reproduced below for convenience):

“Addressing our third research question, whether the strength of identified neural representations relate to behavioral transfer, we found a positive relationship between decoding strength and experience probe performance that was numerically larger for the structurally relevant (6-bridge) graph than for the irrelevant (4-cycle) graph, though this difference did not reach significance; no corresponding relationship was evident for inference probes.” Thus, a behavioral accuracy group difference in predicting successive states for the 6-bridge inference probe performance was of negligible magnitude and did not align with the robust effect observed for experience probes (Fig. 2D), where the latter replicates and extends a previous finding using a 6-state cycle graph and predicted by computational simulations using successor feature models (Luettgau et al., 2024). We speculate that the disparity between probe types is likely due to experience probes and inference probes engaging dissociable cognitive processes – the former relying on predictive representations acquired from experience, the latter relying on an ability to perform mental operations on learned representations of independent feature transitions. This may increase the likelihood of errors due to complexities of the inferred state spaces. However, the observed differences could also relate to previously reported effects of explicit knowledge on performance levels (Luettgau et al., 2024) or be driven by capacity limitations in working memory taxing larger subprocesses more strongly (Collins et al., 2017; Collins & Frank, 2012). “It is also likely that structural knowledge is not acquired uniformly across compounds. Because abstract roles are learned gradually and with uncertainty, role inference is inherently context-dependent: the role of a given stimulus is not inferred in isolation, but in relation to the compound within which it appears. When one element of a compound is already known with high confidence, the role of the second element can be inferred more reliably; when both elements are themselves uncertain, inference becomes less precise. Learning precision may therefore vary across stimulus pairings depending on their frequency, co-occurrence statistics, and position within a sequence, and we would expect corresponding variability in participants' ability to infer dynamical roles, and hence to predict outcomes, across different compound types. This means that an MEG signal, which indexes role-based representational structure specifically for experienced compounds, most directly reflects knowledge precision for those items. A correlation with inference-probe accuracy requires an additional inferential step, from experienced to novel compounds, introducing noise proportional to the uncertainty in the learned representations. In principle, better structural knowledge about experienced compounds should support better generalisation to novel ones, but we might be insufficiently powered to detect this weaker relationship. We therefore interpret an absence of a significant correlation for inference probes not as inconsistent with a structural scaffolding account, and suggest that a null result here should be interpreted with caution rather than as evidence against it. More broadly, an absence of a strong correlation between aggregate neural decoding measures and aggregate inference-probe performance should not itself be taken as evidence against abstract learning. Inference performance is likely supported by multiple sources of information, including partial structural knowledge and heuristic strategies, whereas neural decoding captures the stability of representational geometry at the population level. The localizer RSA results reported above demonstrate that abstract role representations are present in the neural signal, even though their task-dependent expression may not always be directly mirrored in inference-probe behavior.”

(3) The authors write, "we observed a qualitative pattern indicative of increased neural similarity between stimuli that adhered to the same underlying subprocess across task phases. (...) There was a statistically significant interaction effect of condition x graph factor spanning approximately 300 - 680 ms post-stimulus onset". I conclude there was no significant main effect of graph factor, but the relevant statistics are not reported. The authors should report and discuss the complete statistics.

Thank you for this comment. The reviewer is correct in their conclusion that the main effects were not significant and we agree the main effect of graph factor and group (as well as their significance) should be reported. We now do so in the figure caption of Figure 3D, as well as in the results section. The section reads as follows:

We did not observe prior learning group and graph factor main effects (all PFWE > 0.118, non-parametric permutation test).

(4) The RSA is performed on highly aggregated data (the PCs that explained 80% of the variance). Could the authors include their rationale for this choice (e.g. over-analysis of sensor-level data)? In case sensor-level analyses have been conducted as well, maybe there are comparisons or implications of the chosen approach that are useful to mention in the discussion. The authors should provide the average and distribution of the number of PCs underlying their analyses.

We thank the reviewer for raising this important methodological concern. We agree that the use of PCA-based dimensionality reduction in RSA requires further justification. Our primary motivation for using PCA, and retaining components that jointly explain 80% of the variance, was based on denoising rather than aggregation per se. Sensor-level MEG data are high-dimensional and highly correlated, and representational analyses that operate directly on the full sensor space may be susceptible to noise amplification and overfitting, particularly when estimating distance measures across time. Retaining components up to a fixed variance threshold is a widely used approach in MEG decoding and RSA to preserve the dominant signal structure while attenuating sensor-specific noise. Importantly, this procedure discards only the lowest-variance 20% of the signal and on this basis does not impose strong constraints on the representational geometry.

To address the reviewer’s concern more directly, and to ensure our findings are not driven by the PCA procedure itself, we conducted additional robustness checks. Specifically, we performed sensor-level RSA analyses without PCA, using multiple distance metrics (including L1 and L2 distances). These sensor-level analyses yielded highly similar temporal profiles and statistical effects to the PCA-based results, including for the key contrasts reported in the main text. We now include these results in a new supplementary figure and reference them explicitly in the Results section.

In the revised manuscript, we clarify that PCA was used as a principled denoising step, not as a means of imposing structure on the data, and we explicitly show that our conclusions are robust across analytic choices.

“Importantly, to verify that the chosen PCA approach did not impose artificial structure within the data, or introduce other potential confounds, we also conducted the above analyses on sensor level MEG data. Highly similar results were obtained, with consistent results for different similarity metrics (absolute distance (L1 norm) and Euclidean distance (L2 norm), Supplementary Figure 3)), demonstrating that our results and conclusions are robust across analytic choices.”

Methods

“In addition to the PCA-based feature analysis, we performed a sensor-level RSA. At each time point, we estimated condition-specific activation patterns using a GLM applied separately to each sensor (dummy-coded stimulus identity). RDMs were then computed across stimuli using mean absolute difference (L1 norm) as the primary distance metric. For completeness, we additionally evaluated Euclidean distances (L2 norm), which yielded qualitatively similar results (Supplementary Figure 3).”

(5) While the paper is well-written overall, it would benefit from more explicitly identifying the concrete research question and advancing through the results. The authors state their aim as understanding the "temporal dynamics of compositional generalisation", revealing "at which moment during neural information processing are they assembled". They conclude with "providing evidence for temporally resolved neural dynamics that support compositional generalization" and "we show the neural dynamics (...) presented across different task phases...". It remains somewhat vague what specific insight about the process is provided through the temporal resolution (e.g., is the time window itself meaningful, if so, it should be contextualized; is the temporal resolution critical to dissociate subprocesses). The different task phases -initial learning and transfer- are the necessary conditions to investigate transfer learning, but do not by themselves offer a particularly resolved depiction of the process.

We thank the reviewer for these thoughtful and constructive comments. We agree that in the original version of the manuscript our framing did not sufficiently specify the concrete insight that might be gained from neural data, nor did it clearly delimit the scope of our claims. Our primary research question did not relate to characterizing fine-grained temporal mechanisms or sequential subprocesses underlying compositional generalization (e.g., oscillatory dynamics, replay, or temporally ordered stages of computation). Rather, our goal is to determine whether abstract compositional structural representations are detectable neurally during stimulus processing, and how these representations are shaped by prior learning experience.

We address three specific research questions: whether subprocess-specific representational similarity emerges following learning that is specific to a subprocess experienced during prior learning; whether fine-grained dynamical role representations are acquired during stimulus processing; and whether their strength relates to a behavioral transfer success. Importantly, the time-resolved nature of the analyses is a feature of the method that allows us to track the expression of representational content at a sub-trial timescale, rather than an end in itself. We agree with the reviewer that the temporal resolution does not, in itself, resolve distinct computational subprocesses, nor does it provide a mechanistic decomposition of compositional operations. Accordingly, we have revised the manuscript to more explicitly articulate these three concrete research questions in the Introduction, as well as clarify that the reported time windows should be interpreted as markers of representational availability rather than discrete processing stages. We also tone down any language that might be interpreted as making claims about temporally structured mechanisms. Finally, we agree that the distinction between task phases (prior learning vs. transfer) is not intended to depict a detailed temporal process, but rather to provide the necessary contrast to test whether neural representations reflect abstract structural knowledge that goes beyond direct experience. We have revised the Results and Discussion to make this logic more explicit and to better guide the reader through how each analysis contributes to addressing the three research questions.

We believe these revisions better align our claims with the level of insight the data support and make the contribution of each analysis more legible to the reader.

Reviewer #2 (Recommendations for the authors):

(1) Could the authors explain in the manuscript how the held-out transitions were chosen?

We agree that the stimulus construction and sequence generation logic were not described with sufficient clarity. In the revised manuscript we add an explicit description of how compound images were constructed from two independently varying visual features, each corresponding to one graph factor, and introduced the distinction between directly experienced, implied-but-unobserved, and never-valid transitions earlier in the text, so that the probe logic is easier to follow from the outset.

We reproduce parts of the revised methods section describing the held-out stimulus set below:

“[...] Because sequences were drawn from a subset of the product graph, only a portion of all 24 possible compound images (and their transitions) were encountered directly. Transitions between compound images could thus be: (i) directly experienced in a sequence, (ii) never presented in a sequence but implied by the factorization structure, or (iii) transitions between compound images from different subgraphs, which were never valid. The held-out set of transitions described in (ii) and (iii) between compound stimuli (partially observed during sequence presentations, partially never observed during sequence presentations) provided a context for assessing knowledge of graph factorization.”

(2) It might be easier to follow the results section (without going back to Figure 1) if the mentioning of specific graph factors (6-bridge, 4 cycle) would occasionally be accompanied by their function/condition in the experiment.

Thanks for this suggestion, we have implemented this in the manuscript.

Reviewer #3 (Public review):

Summary:

This study investigates how task components can be learned and transferred across different task contexts. The authors designed two consecutive sequence learning tasks, in which complex image sequences were generated from the combination of two graph-based structural "building blocks". One of these components was shared between the prior and transfer task environments, allowing the authors to test compositional transfer. Behavioral analyses using generalized linear models (GLMs) assessed participants' sensitivity to the underlying structure. MEG data were recorded and analyzed using classifications and feature representational similarity analysis (RSA) to examine whether neural similarity increased for stimuli sharing the same relational structure. The paper aims to uncover the neural dynamics that support compositional transfer during learning.

I found the methods and task design of this paper difficult to follow, particularly the way stimuli were constructed and how the experimental sequences were generated from the graph structures. These aspects would be hard to replicate without some clarification. I appreciate the integration of behavioral and neuroimaging data. The overall approach, especially the use of compositional graph structures in sequence learning, is interesting and could be used and revised in further studies in compositionality and transfer learning. I appreciated the authors' careful interpretation of their findings in the discussion. However, I would have liked a similar level of caution in the abstract, which currently overstates some claims.

We thank the reviewer for a positive evaluation coupled with helpful suggestions to improve the clarity of our presentation. We are particularly pleased the reviewer found the integration of behavioral and neuroimaging data, the compositional graph structure approach, and our interpretation of findings in the discussion to be particular strengths of the manuscript.

We address the two specific concerns raised below.

We agree that the stimulus construction and sequence generation logic were not described with sufficient clarity. In the revised manuscript we have: (i) added an explicit description of how compound images were constructed from two independently varying visual features, each corresponding to a single graph factor; (ii) defined the Cartesian product graph operationally, clarifying also that transitions between compound images are valid when one factor changes state while the other remains fixed; (iii) included a worked example tracing a sample sequence through both factors; and (iv) introduced the distinction between directly experienced, implied-but-unobserved, and never-valid transitions earlier in the text, so that the probe logic is easier to follow from the outset.

We reproduce parts of the revised methods section describing stimulus construction below:

“Compound images were constructed by overlaying two independently varying visual features drawn from separate feature sets. Each feature set corresponded to a single graph factor, such that the state of each graph factor independently determines one feature of the compound image. For example, a compound image in state (A, 3) would display feature A from the cyclic factor and feature 3 from the path factor, superimposed or juxtaposed into a single image.

The set of all compound images and their transitions was defined by the Cartesian product of two graph factors: transitions between compound images were valid if, and only if, one factor alone changed state according to its own transition rules while the other factor remained fixed.

Observed sequences of image compositions composed from 10 individual features. Each sequence consisted of 8 compound images with 12 compound images in total across sequences.

[...] For instance, in condition 1, a valid sequence might proceed: (A,1) → (A,2) → (A,3) → (B,3) → (C,3) → (C,4) → (D,4) → (D,5), where each step reflects a transition in either the cyclic (letter) or path (number) factor, but never both simultaneously.

[...] Because sequences were drawn from a subset of the product graph, only a portion of all 24 possible compound images (and their transitions) were encountered directly. Transitions between compound images could thus be: (i) directly experienced in a sequence, (ii) never presented in a sequence but implied by the factorization structure, or (iii) transitions between compound images from different subgraphs, which were never valid. The held-out set of transitions described in (ii) and (iii) between compound stimuli (partially observed during sequence presentations, partially never observed during sequence presentations) provided a context for assessing knowledge of graph factorization.”

We thank the reviewer for flagging the mismatch between the strength of interpretations made in the abstract and discussion section. We have revised the abstract to bring the language in line with the level of caution exercised in the discussion, avoiding overstated interpretations of the findings.

The revised abstract is reproduced below:

“A human ability to adapt to the dynamics of novel environments relies on abstracting and generalizing from past experiences. Previous research has focused on how humans generalize from isolated sequential processes, yet we know little about mechanisms that enable adaptation to more complex dynamics, including those that govern much everyday experience. Here, using a novel sequence learning task based on graph factorization, coupled with simultaneous magnetoencephalography (MEG) recordings, we ask whether reuse of experiential "building blocks" enable inference and generalization. Behavioral results were consistent with participants decomposing task experience into sub processes, abstracting their dynamical structure away from their sensory specifics and transferring these to a new task environment. Neurally, this transfer was associated with a learning-induced, condition-specific, increase in neural similarity among stimuli conditional on their structural role in abstract sub processes that were shared across task phases. Consistent with this, a complementary dynamical role decoding analysis revealed enhanced neural decodability for stimuli sharing identical structural transition types across experiential contexts, specifically when prior experience included the relevant graph structure. Decoding strength for these role representations was positively related to behavioral success in sub process knowledge transfer, a relationship that will require future independent replication. These findings provide neural evidence consistent with the idea that a structural scaffolding mechanism supports generalization of experience to new contexts.”

(1) While the introduction mentions brain areas implicated in the low-dimensional representation of task knowledge, the current study uses M/EEG and does not include source reconstruction. As a result, the focus is primarily on the temporal dynamics of the signal rather than its spatial origins. Although I am not suggesting that the authors should perform source reconstruction in this study, it would strengthen the paper to introduce the broader M/EEG literature on task-relevant representations and transfer. The same applies to behavioral studies looking at structural similarities and transfer learning. I encourage the authors to integrate relevant literature to better contextualize their results.

Duan, Y., Zhan, J., Gross, J., Ince, R. A. & Schyns, P. G. Pre-frontal cortex guides dimension-reducing transformations in the occipito-ventral pathway for categorization behaviors. Current Biology 34, 3392-3404 (2024).

Luyckx, F., Nili, H., Spitzer, B. & Summerfield, C. Neural structure mapping in human probabilistic reward learning. eLife 8, e42816 (2019). (This is in the references but not in the text).

Zhang, M. & Yu, Q. The representation of abstract goals in working memory is supported by task-congruent neural geometry. PLoS biology 22, e3002461 (2024).

L. Teichmann, T. Grootswagers, T. Carlson, A.N. Rich Decoding digits and dice with magnetoencephalography: evidence for a shared representation of magnitude Journal of cognitive neuroscience, 30 (7) (2018), pp. 999-1010

Garner, K., Lynch, C. R. & Dux, P. E. Transfer of training benefits requires rules we cannot see (or hear). Journal of Experimental Psychology: Human Perception and Performance 42, 1148 (2016).

Holton, E., Braun, L., Thompson, J., Grohn, J. & Summerfield, C. Humans and neural networks show similar patterns of transfer and interference during continual learning (2025).

We thank the reviewer for providing these helpful suggestions. We have taken these references on board and now introduce these findings in the introduction of the manuscript (reproduced below for convenience):

“In parallel, M/EEG studies have shown that abstract, format-independent representations can emerge dynamically over time. For example, multivariate analyses of MEG data demonstrate cross-decoding of numerical magnitude across distinct symbolic formats (e.g., digits and dice), indicating a shared, format-invariant representation that unfolds with distinct temporal dynamics (Teichmann et al., 2018). More broadly, M/EEG evidence suggests that task-relevant information can be dynamically prioritized, compressed, and reformatted, indicative of a rapid temporal evolution of abstract and behaviorally relevant representations even when spatial localization remains coarse. Recent MEG data suggests that high-dimensional sensory inputs are progressively transformed into lower-dimensional, task-relevant, feature manifolds across distinct processing stages, reflecting dynamic gating and reformatting of information in support of flexible categorization (Duan et al., 2024). Complementary EEG–fMRI evidence also indicate abstract task goals are encoded in a low-dimensional neural geometry that emerges in frontal cortex and communicated to posterior regions to guide implementation of stimulus-specific representations, with the fidelity of this geometry predicting behavioral performance (Zhang & Yu, 2024). Likewise, converging behavioral and computational data indicates successful generalization depends on detecting and encoding abstract relational structure rather than stimulus surface features. In effect, training enables transfer when task phases share an underlying rule or abstract relationship, even across modalities, but not when an overlap is purely perceptual (Garner et al., 2016).”

“At the same time, reuse of shared abstract representations introduces a computational trade-off, such that overlapping codes that facilitate transfer can also induce interference, as observed in both humans and artificial neural networks (Holton et al., 2025). However, while there is now much work elucidating how learned representations are generalized, it remains unclear whether and how abstracted structural representations are expressed neurally during ongoing stimulus processing, and how they are shaped by prior structural experience. Thus there is a need to characterize not only where abstract representations are located in the brain but also how they dynamically unfold and are reused across contexts in support of compositional generalization.”

(2) I found it interesting that the authors chose to perform PCA for dimensionality reduction prior to conducting RSA; however, I haven't seen such an approach in the literature before. It would be helpful to either cite prior studies that have employed a similar method or to include a comparison with more standard approaches, such as sensor-level RSA or sensor-searchlight analysis.

(3) Connected to the previous point, the choice to use absolute distance as a dissimilarity measure is not justified. How does it compare to standard metrics such as correlation distance or Mahalanobis distance? The same applies to the use of Kendall's tau.

We thank the reviewer for raising these methodological concerns and agree methodological choices should be explicitly motivated and justified. Our primary motivation for using PCA, and retaining components that jointly explain 80% of the variance, was denoising. Sensor-level MEG data are high-dimensional and highly correlated, and representational analyses that operate directly on the full sensor space may be susceptible to noise amplification and overfitting, particularly when estimating distance measures across time. Retaining components up to a fixed variance threshold is a widely used approach, both in MEG decoding and RSA, to preserve the dominant signal structure while attenuating sensor-specific noise. Importantly, this procedure discards only the lowest-variance 20% of the signal and therefore does not impose strong constraints on the representational geometry.

To address the reviewer’s concern regarding methodological choices and what this means for the conclusions drawn more directly, and to ensure our findings are not driven by specific analytic choices, we conducted additional robustness checks, availing of more “standard” approaches. Specifically, we performed the same RSA on localizer tasks but using sensor-level data without PCA, employing multiple distance metrics (including absolute distance/L1 norm and Euclidean distance/L2 norm). These similarity metrics are commonplace in RSA, providing linear, per-dimension differences between neural patterns (L1) or robust small outlier differences along individual dimensions compared to squared differences (Euclidean/L2), providing simple and interpretable similarity metrics.

These sensor-level analyses yielded highly similar temporal profiles and statistical effects to the PCA-based results, including the key contrasts reported in the main text. We now include these results in a new Supplementary Figure and reference them explicitly in the Results section.

In the revised manuscript, we clarify that PCA was used as a principled denoising step, not as a means of imposing structure on the data, and explicitly show that our conclusions are robust across analytic choices.

“Importantly, to verify that the chosen PCA approach did not impose artificial structure within the data, or introduce other potential confounds, we also conducted the above analyses on sensor level MEG data. Highly similar results were obtained, with consistent results for different similarity metrics (absolute distance (L1 norm) and Euclidean distance (L2 norm), Supplementary Figure 3)), demonstrating that our results and conclusions are robust across analytic choices.”

Methods

“In addition to the PCA-based feature analysis, we performed a sensor-level RSA. At each time point, we estimated condition-specific activation patterns using a GLM applied separately to each sensor (dummy-coded stimulus identity). RDMs were then computed across stimuli using mean absolute difference (L1 norm) as the primary distance metric. For completeness, we additionally evaluated Euclidean distances (L2 norm), which yielded qualitatively similar results (Supplementary Figure 3).”

Our choice of Kendall’s tau rank correlation was motivated by its common use for linking neural and theoretical RDMs (e.g., Luyckx et al., 2019 eLife; Nili et al., 2014 PLoS CB). We have now added these citations to the manuscript.

(5) The analysis described in the "Abstract representation of dynamical roles in subprocesses" does not appear to convincingly test the stated prediction of a structural scaffolding account. The authors hypothesize that if structure and dynamics from prior experiences are repurposed, then stimuli occupying the same "dynamical roles" across different sequences should exhibit enhanced neural similarity. However, the analysis seems to focus on decoding transitions rather than directly assessing representational similarity. Rather, this approach may reflect shared temporal representation in the sequences without necessarily indicating that the neural system generalizes the abstract function or position of a stimulus within the graph. To truly demonstrate that the brain captures the dynamical role across different stimuli, it would be more appropriate to directly assess whether neural patterns evoked by stimuli, in the same temporal part of the sequence, with shared roles (but different visual identities) are more similar to each other than to those from different roles.

We thank the reviewer for this careful and constructive critique and analytical suggestion. The reviewer is correct that in the bridge graph traversal, structural roles map onto fixed serial positions within a sequence, meaning that same-role stimulus pairs also tend to share the same temporal position in the sequence. This is a potential confound: neural similarity between same-role stimuli could in principle reflect similarity related to time-in-sequence rather than an abstract structural role per se.

The original role-based RSA does not fully resolve this concern, and we have now conducted, based on the reviewer’s suggestion, an additional analysis that directly addresses it. Rather than comparing stimuli that share a structural role, we examine whether the neural representation of a single central node stimulus is similar across its two distinct serial positions within the prior and transfer learning sequences. Specifically, in the bridge graph traversal, each central node appears twice per sequence: the left central node occurs at steps 1 and 4, the right central node occurs at steps 5 and 8. We estimate neural patterns for each central node separately at its first and second occurrence, using occurrence-specific GLMs, and then compute cross-phase similarity between prior and transfer learning: the neural pattern evoked by a central node at its first occurrence in prior learning is compared to its pattern at the second occurrence in transfer learning, and vice versa.

For the 6-bridge prior group, whose prior learning also involved a bridge graph, central nodes were identified using the same bridge-template positions (steps 1/4 and 5/8) in both prior and transfer learning phases. For the 4-cycle prior group, whose prior learning involved a line graph rather than a bridge graph, central nodes in the prior phase were identified using degree-based role assignment (the two nodes with the highest degree that are not boundary or intermediate nodes), ordered by first appearance in the prior trial sequence. Transfer learning central nodes were identified from the bridge graph template in both groups, since transfer learning always involved a bridge graph. The group comparison thus tests whether cross-phase similarity between central node representations is specific to participants whose prior experience included a bridge graph relative to participants whose prior experience involved a structurally different graph, for whom "central" nodes in prior and transfer are central in qualitatively different senses. This approach directly controls for the time-in-sequence confound, since the same node is compared across different serial positions rather than comparing different stimuli that share a role and therefore also share a sequence position.

We compared this cross-phase similarity between the 6-bridge prior and 4-cycle prior groups. We observe a significant group difference at a late stage of the trial (approximately 1.125–1.25 sec post-stimulus onset, P^FEW = 0.043, two-sample non-parametric permutation test, one-tailed), with additional differences at earlier time points that did not survive correction for multiple comparisons (0.125 sec: t = 2.18, p = .034; 0.79 sec: t = 2.84, p = .007). This indicates increased neural similarity for central node representations across phases in participants who experienced these roles consistently during prior learning.

We wish to be entirely transparent, however, about two limitations of this additional analysis with respect to the original dynamical role decoding results reported in Figure 4. First, the temporal profile of the cross-phase similarity effect does not perfectly overlap with the time windows identified in the original decoding analysis, which limits the strength of the convergence argument. We therefore cannot fully rule out a possibility that the earlier decoding effects partly reflect temporal position within the sequence rather than abstract structural role coding per se. Second, this analysis is necessarily based on a smaller and less variable set of comparisons than either the original decoding analysis or the role-based RSA, since the bridge graph contains only two central nodes whose repeated occurrences can be directly compared in this way. This limits the statistical power of the analysis and our ability to draw strong conclusions from it in isolation. We acknowledge both limitations explicitly in the revised manuscript. Nonetheless, the observation of a group-specific effect in the cross-phase analysis, which by design controls for serial position, provides some support for the structural scaffolding account, and the late corrected cluster suggests that role-consistent representations do emerge across learning phases.

In addition to this online analysis, we conducted a parallel role-based RSA on data from the localizer task. This localizer-based analysis examines representational changes from PRE to POST learning for stimuli that share the same structural role within the relevant sub-process graph structures. We find a cluster-based permutation-corrected interaction effect between prior learning group and graph factor, indicating that representational similarity increases selectively for stimuli sharing the same structural role, rather than uniformly for all stimuli associated with a given graph. Together with the localizer-based RSA results, we believe these converging analyses strengthen the overall interpretation, while we acknowledge the temporal confound as a remaining limitation that future work with designs explicitly counterbalancing serial position across roles could address more definitively. We reproduce below the main text results, supplementary methods and Supplementary Figure (Supplementary Figure 4) detailing this complimentary analysis.

Main manuscript

“To further test the robustness of the above effect, and to assess whether abstract dynamical roles are reflected in neural representational geometry during task performance, we conducted a complementary cross-phase representational similarity analysis. This analysis addresses directly whether neural representations of central nodes are stable across their distinct serial positions within a sequence, an expected property if representations reflect abstract structural identity rather than time-in-sequence. Specifically, for each participant we estimated neural patterns for each central node separately at its first and second occurrence (phase) within the sequence traversal, using occurrence-specific GLMs, and computed cross-phase similarity between prior and transfer learning phases. This approach controls for a potential time-in-sequence confound inherent in role-based comparisons, since now, the same functional node is compared across different serial positions (rather than comparing different stimuli with a common sequence position, by virtue of sharing role). Consistent with the decoding results, we observed increased cross-phase similarity in participants with prior experience of Component 6 relative to those with prior experience of Component 4 (Supplementary Figure 4). Specifically, a significant group difference was observed at a late stage of the trial (1.125–1.25 sec post-stimulus onset, P_FWE = 0.043, two-sample non-parametric permutation test, one-tailed), with additional differences at earlier timepoints that did not survive correction for multiple comparisons (0.125 sec: t = 2.18, p = .034; 0.79 sec: t = 2.84, p = .007). These effects indicate increased neural similarity for central node representations across phases in participants who experienced these roles consistently during prior learning. We consider these results complementary to the main analyses and interpret them with caution given that the group difference was only corrected for multiple comparisons at the late cluster. Importantly, the temporal profile of the cross-phase similarity effect does not perfectly overlap with the time windows identified in the original dynamical role decoding analysis, which limits the strength of the convergence argument. We therefore cannot fully rule out the possibility that the earlier decoding effects reported in Figure 4 partly reflect temporal position within the sequence rather than abstract structural role coding per se. We additionally note that this analysis is based on a smaller and less variable set of comparisons than either the original decoding analysis or the role-based RSA, since the bridge graph contains only two central nodes whose repeated occurrences can be directly compared in this way, limiting its statistical power in isolation. Nonetheless, the observation of a group-specific effect in the cross-phase analysis which directly controls for serial position provides support for the structural scaffolding account, and the late corrected cluster suggests that role-consistent representations do emerge across learning phases, albeit potentially at a later stage of processing than the decoding results alone would suggest.”

Supplementary Information

“Cross-phase representational similarity analysis

Complementary to the decoding analysis in Figure 4, we conducted a cross-phase representational similarity analysis (RSA) to test whether neural representations of central nodes were stable across their distinct serial positions within a sequence, a property expected under abstract structural role coding but not under serial position coding. We focused on central nodes of the 6-state graph, as these nodes appear twice within each sequence traversal of the bridge graph: the left central node occurs at steps 1 and 4, the right central node occurs at steps 5 and 8, allowing first and second presentations to be dissociated.

Structural roles were assigned separately for prior and transfer learning phases. For line graphs (experienced by the Condition 4 during prior learning), central nodes were identified from node degree in the adjacency matrix (boundary: degree 1; intermediate: neighbors of boundary; central: remaining nodes), and the two central nodes were ordered by first appearance in the trial list. For bridge graphs, central nodes were identified from the predefined 8-step traversal template.

At each time point and sensor, condition-specific activations were estimated using occurrence-specific GLMs: one GLM fitted to trials corresponding to the first occurrence of each number in the trial list, and one fitted to trials corresponding to the second occurrence. Component 6-specific beta estimates were extracted from each GLM separately, yielding four sets of neural patterns per subject: prior-phase first occurrence, prior-phase second occurrence, transfer-phase first occurrence, and transfer-phase second occurrence.

Cross-phase representational dissimilarity was then computed using an L1 distance metric (mean absolute difference across sensors) across four cross-presentation pairs: Left central (prior first, transfer second), left central (prior second, transfer first), right central (prior first, transfer second), and right central (prior second, transfer first). These pairings compare the same node across different serial positions and different learning phases, directly controlling for time-in-sequence as a potential confound. The mean L1 distance across the four pairs constituted the cross-presentation dissimilarity index at each time point, where lower values indicate greater neural similarity. Timecourses were baseline-corrected by subtracting the pre-stimulus mean (timepoints 1–25, corresponding to −250 to 0 ms) per participant, and analyses were restricted to post-stimulus timepoints. Group differences between Condition 6 and Condition 4 participants were assessed using a two-sample non-parametric cluster permutation test (cluster-forming threshold p = 0.10, cluster-level alpha = 0.05, 1,000 permutations, one-tailed, consistent with the directional prediction that Condition 6 participants would show greater cross-phase neural similarity for central nodes). The results are presented in Supplementary Figure 4.”

(4) In the following section, the authors correlate decoding accuracy with participants' behavioral performance across different conditions. However, out of the four reported correlations and the additional comparison of differences between conditions, only one correlation and one correlation difference reach significance, and only marginally so. The interpretation of this finding should therefore be more cautious, especially if it is used to support a link between neural representations and behavior. Additionally, it is possible that correlation with a more clearly defined or targeted neural signature, more directly tied to the hypothesized representational content, could yield stronger or more interpretable correlations.

We agree with the reviewer that the reported brain-behavior correlations should be interpreted cautiously. Only one of the four correlations reached significance, with effect sizes of medium magnitude. However, we emphasize this correlation is significant when corrected for multiple comparisons for two tests, experience and inference probes (ɑ = 0.025). Additionally, it is important to note, we did not expect all four correlations to be significant. The conditions differ in the extent to which behavior is predicted to depend on the specific neural representation indexed by the decoding analysis, and only a subset of conditions are theoretically expected to show a brain–behavior relationship. The absence of significant correlations in the remaining conditions is therefore not inconsistent with our account. For example, we did not expect the two 4-cycle correlations (depicted in green, Fig. 4C) to be significant.

We agree with the reviewer that the reported brain-behavior correlations should be interpreted cautiously, and have revised the manuscript to reflect a more measured interpretation. We note that the correlation value reported in the revised manuscript (ρ = .48, p = .016) differs slightly from the originally submitted version (ρ = .41, p = .041), due to a correction in the timepoint-averaging window used to derive the decoding strength measure. We consider the revised value the authoritative one and have updated all relevant text accordingly.

Only one of the four correlations reached significance, with an effect size of medium magnitude. We would not characterise this correlation as marginal: it survives correction for multiple comparisons across the two theoretically motivated tests (experience and inference probes; corrected α = 0.025), and a medium-magnitude Spearman correlation (ρ = .48) in an individual-differences analysis with n = 25 is consistent with a meaningful brain-behavior relationship, even if the sample size limits the precision of the estimate. We agree that independent replication is needed to establish robustness.

Additionally, it is important to note that we did not expect all four correlations to be significant. The conditions differ in the extent to which behavior is predicted to depend on the specific neural representation indexed by the decoding analysis, and only a subset of conditions are theoretically expected to show a brain–behavior relationship. The absence of significant correlations in the remaining conditions is therefore not inconsistent with our account. For example, we did not expect the two 4-cycle correlations (depicted in green, Fig. 4C) to be significant, since the 4-cycle-prior group did not experience the bridge graph structure during prior learning and therefore would not be expected to show the same alignment between dynamical role representations and transfer learning performance.

In any event, based on the reviewer’s (and comments from other reviewers about these correlations), we have revised the manuscript to tone down the interpretation of these results (reproduced below):

“These findings are consistent with, though not conclusive evidence for, dynamical role representations conveying behavioral benefits. Speculatively, such knowledge representation might enable individuals to constrain their predictions of successive states. For example, upon transitioning to a bridge node one can predict that the successor state will involve "the other side of the bridge". While we acknowledge that the correlation results appear inconsistent across experience and inference probes, it is important to consider that our MEG classifiers were trained and tested on experienced transitions alone, such that enhanced classification accuracy is more reflective of a neural representation of experienced transitions. Under this assumption, the MEG classifier would more closely align with behavioral accuracy for the experience probes (testing actually experienced transitions) than for the inference probes (testing never experienced but only implied transitions on the graph). See Discussion for further elaboration of this point, including why this asymmetry is expected under a model of gradual, imperfect structural learning.

The observed correlation is also consistent with a general learning-ability account, whereby higher-ability participants both better discover the Component 6 structure (that happens to be shared) across sessions and show higher behavioral accuracy overall. For example, higher-ability participants may rediscover this structure during transfer, without necessarily benefitting from having been exposed to it during primary learning. This ability-based account predicts that decoding strength should also relate to Component 4 accuracy, and that Component 4 and Component 6 accuracy should correlate within each prior learning group. Neither prediction was consistently supported (Supplementary Figure 5): The Component 4 decoding strength and Component 4 correlation was not significant (ρ = .38, p = .071), and did not differ significantly from the Component 4 decoding strength and Component 6 correlation (Steiger's test, p = .656); accuracy correlations between Component 4 and Component 6 were significant in only one prior learning group for each probe type, with no significant between-group differences (all p > .29).

Given this inconsistent pattern, we consider the general-ability account unsupported, though our low per-condition sample size limits power to rule it out. We therefore treat the brain-behavior correlation as selective to Component 6 experience probes in this sample, and treat it as supportive rather than primary evidence for a link between role representations and transfer, pending independent replication.”

We agree that a more targeted neural signature could in principle yield a more interpretable correlation with behavior. Our interpretation of the reviewer's comment is that this implicitly requires a measure that captures representational content at the level of individual trials or items, for example, a trial-by-trial estimate of how strongly a given stimulus is represented in its abstract structural role, which could then be correlated with individual participants' behavioral performance. Our current decoding measure does not provide this: it indexes classification accuracy averaged across all trials of a given transition type, yielding a single scalar value per participant per timepoint rather than a trial- or item-level representational estimate.

Computing such a trial-level measure from our data would require a fundamentally different analysis approach, for example, single-trial decoding confidence scores or RSA-based measures of individual stimulus representational fidelity, which goes beyond what our current classifier-based pipeline and data structure can deliver. We have instead conducted additional analyses that more directly index neural representational content (role-based representational similarity analyses, reported in the revised manuscript), which provide converging support for the proposed computational account.

Minor Comments:

“During preprocessing, sensors were excluded based on an identified noise level. However, the authors do not specify the threshold used to define this noise level, nor do they report how many sensors were excluded per participant. It would be helpful to have these details. Additionally, it is unclear why the authors opted to exclude sensors rather than removing noise with MaxFiltering or interpolating bad sensors. Finally, the authors should report how many trials were discarded on average (and standard deviation) per participant.”

We thank the reviewer for these comments. We have updated the methods section to address the points raised.

Regarding the noise threshold and number of excluded sensors/trials: sensors were excluded using the default osl_detect_artefacts settings, which apply a Generalised Extreme Studentised Deviate (GESD) test at a significance level of 0.05. On average across all MEG runs and participants, 8.67 sensors (SD = 7.36) and 9.13 trials (SD = 11.46) were excluded. These details have been added to the methods section.

Regarding the choice to exclude sensors rather than applying MaxFilter or interpolation: MaxFilter was not applicable here as our data were acquired on a CTF system, for which MaxFiltering is not designed. Sensor interpolation was not performed as bad channels are excluded prior to ICA decomposition following standard OSL pipeline practice. Given that excluded sensors represented on average ~3% of the total 273 sensors, we do not expect this to have meaningfully affected our results.

The updated methods section now reads as follows:

“On average across all MEG runs and participants, 8.67 sensors (SD = 7.36) and 9.13 trials (SD = 11.46) were excluded (using default osl_detect_artefacts settings; channel significance level for Generalised Extreme Studentised Deviate = 0.05). We did not apply MaxFilter as our data were acquired on a CTF system, for which MaxFiltering is not designed. Sensor interpolation was not performed as bad channels are excluded prior to ICA decomposition following standard OSL pipeline practice; given that excluded sensors represented on average ~3% of the total 273 sensors, we do not expect this to have meaningfully affected the results.”

Reviewer #3 (Recommendations for the authors):

(1) The manuscript seems to use the terms generalization, transfer, compositionality, and compositional generalization somewhat interchangeably. While I appreciate that both compositionality and transfer learning are central to the task design, I believe it's important to distinguish these concepts more clearly. Specifically, generalization typically refers to the ability to apply learned structure within a task to novel but similar instances, whereas transfer involves applying learned components or representations across different tasks or contexts. Clarifying these distinctions - ideally with explicit definitions early in the introduction - would help avoid confusion and better situate the contribution of this work within the broader literature.

(2) The manuscript frequently refers to abstract knowledge or abstract representations. However, I would argue that abstract knowledge is typically characterized by its ability to generalize or transfer across different tasks or domains. In the current paradigm, while the structural relationships between stimuli change, the task demands and sensory modalities remain constant. It would strengthen the conceptual clarity of the paper if the authors could more carefully define what they mean by "abstract".

We thank the reviewer for these suggestions. We agree that “abstract” can carry different meanings across the literature. We have now added an explicit definition to the introduction clarifying our usage. We use 'abstract' to refer to representations that are invariant to surface sensory features while capturing relational structure, consistent with findings in a representation learning literature (e.g., Bernardi et al., 2020; Behrens et al., 2018). While the reviewer raises the valid point that task demands and sensory modality remain constant across learning phases, we highlight that the stimuli themselves are entirely novel in the transfer phase, such that any representational similarity must reflect relational rather than perceptual overlap.

We have added explicit definitions of abstract, generalization, transfer, and compositional generalization to the introduction, clarifying how each term applies to our task design and how they relate to one another. We have also aimed for more consistent usage throughout the manuscript.

This added paragraph in the Introduction reads as follows:

“Throughout this work, we use "generalization" to refer to the ability to apply learned relational structure to novel stimulus compositions within the same task context, and "transfer" to refer to the reuse of (abstracted) representations across distinct task contexts or learning phases. Note we use “abstract” to refer to representations that are invariant to the sensory specifics of individual stimuli, capturing relational structure (e.g., the role a stimulus occupies within a graph) rather than surface features. Our task is structured compositionally in that every experienced compound stimulus is the joint product of two simultaneously evolving subprocesses, while the specific compound encountered during transfer learning is never observed during prior learning. We use 'decomposition' and 'transfer' to refer to the abstraction and reuse of a single such subprocess across learning phases, and reserve “compositional generalization” for the broader phenomenon whereby task performance depends on appropriately decomposing and recombining structural knowledge, a capacity our design requires of participants. Here we acknowledge that our study speaks most directly to decomposition and transfer of individual structural components rather than to the act of recombination itself.”

(3) The supplementary materials include a section on replay analyses, but it is unclear how these analyses relate to the main text. I could not find a corresponding discussion or reference to replay in the results or discussion sections.

We thank the reviewer for flagging this. The replay analysis was referenced in the Discussion of the previous version of the manuscript. To make this analysis more visible, we have also added a brief summary of the null replay result to the Results section, with a pointer to the Supplementary Results where the full analysis and discussion of limiting factors are reported.

Author response:

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

eLife Assessment:

This valuable study addresses a critical question regarding the role of a subpopulation of cortical interneurons (Chrna2-expressing Martinotti cells) in motor learning and cortical dynamics. However, despite the inclusion of interesting behavioral and imaging data, significant limitations remain, even after revision, in the design of the motor learning task and the associated data analyses. As a result, the presented data are incomplete to support the central conclusions.

We appreciate the valuable feedback. To address these concerns, we have rephrased all conclusions to explicitly focus on motor execution consolidation rather than learning, as our task design inherently emphasizes performance refinement over acquisition. This reframing is now fully supported by compelling evidence from our data and analysis, demonstrating that Mα2 cell activation reduces pyramidal cell population plasticity and improves motor execution.

Public Reviews:

Reviewer #1 (Public review):

In line 331, the authors refer to session 5 as “training,” describing it as the final spoon session, and session 6 as “re-training,” because it is the first session in which the pellet is presented on the plate rather than on the spoon. However, in Fig. 1F-H, even in the Ctrl group, it is clear that the performance drops significantly in session 5, which is supposed to be the easiest session before switching to the more difficult plate condition.

As described in the methods, the task is made progressively harder (as evidenced by the success ratio curve), therefore a lower performance in session 5 (the hardest spoon session) is expected, as now explicitly stated in the results (lines 816-825).

In the classic pellet-reaching task, the spoon sessions would typically be considered “shaping”, while the plate sessions would represent the actual training phase. However, in this manuscript, the authors still insist on referring to session 2 as “learning” and session 5 as “training.” I don’t understand the difference between session 2 and session 5, especially when session 5’s performance is lower than session 2 (even in Fig 1H when you compare succ ratio).

The experiments were designed to investigate the effect of Ma2 cell activation on learning and training outcomes. As we wanted to compare completely naive mice with mice that had been trained and that had learned the task, we included the first sessions with the spoon in our analysis. In many other studies or experimental set-ups those sessions would have been considered shaping. The reason for this design is that we did not want to miss early changes related to training and learning that could have a great impact on the final outcome, as most dendritic spines that correlate with learning are formed after the initial training session and are maintained in the second training session (10.1016/j.neuron.2021.07.030). During pilot studies, several different strategies were tested and it was discovered that the mice needed to succeed several times in the initial sessions in order to keep trying. Hence, the pellet presentation needed to be less challenging in the beginning than in the final sessions in which the pellet was presented on the plate. Therefore, as explained above, the task was made progressively harder throughout the session and from session to session, thus mice expectedly had more difficulty in session 5. We agree that the session names could be misleading, particularly in the context of our task design, and therefore changed all session labels to session numbers.

Since session 6 (on the plate) is considered as “retraining,” why don’t the authors present the behavioral results beyond session 6? As a result, it remains unclear whether the animals improved their performance during the retraining phase.

We agree, and now show behavior performance from sessions 1 to 10 for the behavioural group. Mice displayed a clear improvement after session 6, reaching a plateau after session 7 (Figure 1F-H). Unfortunately, due to technical challenges with reattaching the miniscope multiple times and following the same neurons over time, we do not have miniscope data from beyond session 6, which is why we initially only presented behavioural data up to session 6.

Lastly, in Fig. 4B the authors present only the success ratio and claim that performance improves with CLZ application. However, when comparing sessions 8-10 between the Ctrl and Cre+ groups, there already appears to be a baseline difference. CLZ treatment in Cre+ mice seem to bring performance only to the WT level rather than producing a clear improvement beyond baseline.

In the previous version (first submitted), we showed the success rate (number of success per minute), to the same conclusion. Note that our conclusion is supported by the effect of treatment found in Cre+, meaning that Cre+ improved upon CLZ (Ma2 cells increase in excitability) compared to NaCl (No change in Ma2 cell excitability). The control group is a control for the Ma2 cell activation specificity, and as expected it shows no treatment effect (since there is no hM3Dq expression, as already reported, Supplemental Table 1L). Further, the reviewer’s suggestion of a baseline difference between groups is not supported by our data, since no statistical differences were found on these comparisons (t-test eff. size < -1.587; p > 0.293; as already stated in the methods, the absence of significance bars “for any comparison means no significant difference was found”).

Regarding the alignment between imaging and behavior, the authors report ~100 prehensions per minute. However, the calcium imaging traces show fewer than 20-30 spikes over 150 seconds (~2.5 min; Fig. 1E). This discrepancy raises concerns about whether the authors can truly isolate calcium signals corresponding to individual prehension events (either successful ones or multiple combined events for unsuccessful attempts). The manuscript still does not present behavioral data that directly aligns prehension events with calcium imaging activity. Although the authors performed analyses suggesting that prehension-related activity does not systematically alter nonprehension epochs, this claim is difficult to evaluate without seeing the underlying traces. It is therefore unclear how the authors selected the example calcium traces aligned to prehension onset, given that there are more than 100 prehension events per minute.

If we understand this comment correctly, the reviewer presumes that there should be a direct relationship between upper motor neuron activity and prehension activity (i.e. muscle activity). Such one-to-one correspondence between prehension events and calcium transients in individual pyramidal neurons should not be expected.

Upper motor neurons do not fire in a direct, event-by-event relationship with movements. Instead, motor actions emerge from distributed population activity, where individual neurons contribute sparsely and variably. Classical work described in the book Corticospinal function and voluntary movement by Porter and Lemon (1993) show that the relationship between single-neuron firing and muscle contraction is indirect and probabilistic. This circumstance required spike-triggered averaging based on several thousands of recordings to reveal consistent relationships between neuronal firing and motor output, precisely because individual spikes are neither necessary nor sufficient for a movement instance.

Calcium imaging accentuates this dissociation. Calcium signals are a temporally filtered and nonlinear proxy of spiking activity, with limited sensitivity to single spikes and a bias toward burst-like or temporally clustered firing. As a result, many individual action potentials, especially those occurring in isolation, may not generate detectable calcium transients. Therefore, observing fewer calcium events than behavioral actions is expected and does not imply a failure to capture relevant neural dynamics.

Thus, motor cortex representations during skilled behaviors such as prehension are distributed across neuronal ensembles rather than encoded at the level of single neurons. Each prehension recruits a subset of neurons, and each neuron contributes only intermittently across trials. Consequently, the appropriate level of analysis is not event-by-event alignment for individual cells, but rather population-level dynamics (e.g., ensemble activity patterns, dimensionality reduction, or trial-averaged responses aligned to behavior).

We have not selected “example calcium traces aligned to prehension onset”. We performed all quantifications on the average of all trials, and we thus show one example of such traces in Figure I and all average traces in Supplemental Figure 3I. All trials were included, therefore there is no “selection”, as already explained in the methods section (lines 607-611).

Taken together, the apparent discrepancy between behavioral event rate and calcium event frequency reflects known principles of motor cortex coding and calcium imaging limitations, rather than a methodological inconsistency. This explanation is now added to the discussion section (lines 1186-1211).

Regarding the baseline effect analysis (Supplemental Figure 3I), we do not understand the claim that the underlying traces for the quantification shown cannot be seen, when they are explicitly shown in the same figure (Supplemental Figure 3A-E). We agree that the figure legends for Supplemental Figures 2 and 3 were missing the description of the traces shown as average traces of all trials for all neurons, with the shade showing the standard error of the mean. We now added this information to the Supplemental Figures 2 and 3 legends.

In Fig. 1I, the authors also did not address why neural activity during successful trials is already lower one second before movement onset. The longer traces provided do not help to explain this observation or clarify the origin of this pre-movement reduction in activity. It actually further suggests that there may be some artifacts in the imaging that could affect the analysis.

We understand that the example shown in Figure 1I can cause confusion, therefore we chose a clearer example neuron. As explained in the previous comment, no quantifications were made at the trial level, therefore Figure 1I shows the average +SEM of all trials.

Overall, because it remains difficult to understand exactly what the authors are analyzing (and because the definitions of the motor learning stages appear arbitrary) it is difficult to agree with the authors’ conclusion that Ma2s cells reduce PyrN cell assembly plasticity during learning, thereby possibly facilitating already acquired motor skills.

We rewrote our conclusions to better fit our results and thoroughly explained the calcium imaging analysis concerns above. No quantifications (nor claims) were done at single-level trial, and we clearly show the exact traces from where the quantifications were derived (Figure 1E, 1I; Supplemental Figure 2A-H and 3A-H.

Reviewer #2 (Public review):

While the authors addressed some of the concerns raised by the reviewers, several major limitations still exist in the revised manuscript.

(1) I appreciate the authors now showing more measures of the prehension task (total reaches, success reaches/min, and success ratio) and providing more details on the task design. However, it is unclear why the authors chose a task design that is somewhat different from the commonly used approach. Here they increase the distance of the food pellet each session and are thus making the task increasingly harder, whereas commonly the target distance is kept stable (See 10.1038/nature08389 for example). The result is that important readouts of learning (e. g. success rate) thus remain stable, making it impossible to judge if learning has occurred, without a control group of non-trained mice. This makes it impossible to judge if the task is affected by increased Ma2 cell excitability, since there is no reference of how these measurements are supposed to change in a mouse that learns or doesn’t learn the task.

The experiments were designed to investigate the effect of Ma2 cell activation on learning and training outcomes. As we wanted to compare completely naive mice with mice that had been trained and that had learned the task, we included the first sessions with the spoon in our analysis. In many other studies or experimental set-ups, those sessions would have been considered shaping. The reason for this design is that we did not want to miss early changes related to training and learning, that could have a great impact on the final outcome, as most dendritic spines that correlate with learning are formed after the initial training session and are maintained in the second training session (10.1016/j.neuron.2021.07.030). During pilot studies, several different strategies were tested and it was discovered that the mice needed to succeed several times in the initial sessions in order to keep trying. Hence, the pellet presentation needed to be less challenging in the beginning than in the final sessions in which the pellet was presented on the plate. On previous pilot experiments, when the spoon distance was kept stable across sessions, most animals did not perform the task upon switching to the plate position (a large and abrupt increase in difficulty), whereas progressively increasing the difficulty led to more mice reaching for the plate target. We agree that this task design better reflects motor execution than learning, and have stated throughout the manuscript that learning is unaffected. We also reframed conclusions about learned motor execution to better fit our task design.

(2) Regarding the analysis of the calcium imaging data, it is still unclear why the authors cannot report a commonly used dF/F0 or z-score value, as recommended by both reviewers. The authors state the 1 sec time window prior to the prehension cannot be used as a baseline (F0), as there might be preparatory motor activity. In that case an even earlier window (such as -2 to -1sec) or z-scores should be used. The current version relabeling the background subtracted fluorescence signal as dF/F0 is misleading. Relatedly, it is unclear why the authors don’t think the 1 sec window before prehension cannot be used as baseline, but at the same time use the difference in calcium activity before and after prehension onset as a cut-off criterion for defining cells as modulated during prehension and including in the analysis.

As explained in the previous review round, we performed baseline subtraction as described in the methods section: "The baseline components were estimated using a running 8th percentile derived from kernel density estimation over a 250-frame window, and subtracted from each respective trace. Although true F0 estimation is not possible on 1-photon data, the baseline-subtracted trace is here referred to as ΔF/F. The fact that the label ΔF/F is commonly used in 1-photon data is misleading, since studies analyzing miniscope data using the label ΔF/F define F0 as the raw video frame minimum (e.g., 10.1371/journal.pbio.3000584, 10.1111/ejn.70190), mean of “non-spiking” periods for all neurons (e.g., 10.1016/j.crmeth.2025.101221), or providing no F0 definition (e.g., 10.1002/adfm.202511627, 10.3389/fnagi.2025.1550673, 10.1016/j.bpsgos.2025.100531, 10.1038/s41586-025-10096-w), none of which are true F0. We reiterate, as in the previous review round, that any use of the label ΔF/F is technically incorrect, not only here but in any study using 1-photon data.

After the previous review round we defined F0 as the baseline components estimated as described above, which is a much more reliable and standardized measure of baseline components estimation compared to the measures cited above, using an extensively validated algorithm (10.7554/eLife.38173), and labeled our data as ΔF/F since they are already properly scaled, as previously done (10.3389/fnagi.2025.1550673). However, after this discussion, we suggest reverting back to the more correct technical term “ΔF detr.”. This also aligns with previous other similar work (e.g., 10.1073/pnas.2503139122, 10.3389/fnsys.2026.1765204), and that is what our traces (and any traces from any study derived from 1-photon data) actually are.

We searched and found some studies analysing miniscope data that have z-scored fluorescence traces, but none of those provided a clear justification for doing so (e.g., 10.1016/j.isci.2026.115514, 10.1016/j.neuron.2025.07.020). We do not think that z-scoring appropriately scales fluorescence traces, particularly when baseline components are already subtracted. Fluorescence traces exhibit strong positive skewness, characteristic of calcium imaging data where the baseline is stable (after removing baseline components as described above) but transient events create a heavy tail, and z-scoring relies on the mean and standard deviation. In highly skewed distributions, both the mean and standard deviation are strongly influenced by the magnitude and frequency of these transients. Consequently, z-scoring the traces artificially compresses the baseline and distorts the relative amplitude of events, leading to biased comparisons between different cells by penalizing cells according to their own activity (more active cells will have more transients, therefore larger mean, and lower z-scored traces), instead of normalizing to a biologically meaningful scale. This can be easily demonstrated, take for example the signal fragment in Author response image 1.

Author response image 1.

The A panel shows a fluorescence trace from one neuron. If we slice this trace in half (B), the background component is the same, since they are derived from the same cell. If we z-score those halves, the half with higher activity is penalized (C, blue), while the less active half is artificially increased (C, orange). Since both signals are from the same cell, if z-scoring the traces was an appropriate normalization procedure, the differences between them should remain, which is not the case. Therefore, it is clear that z-scoring does not properly scale fluorescence traces for the purpose of comparisons between cells.

Regarding the inclusion criterion, we used the difference between before and after activity precisely to include only neurons related to the task, which does not mean that the "before" epoch is baseline, only that it is not the same as the "after" epoch, as shown by data already included in the manuscript. Further, we already ran the suggested analysis (after/before ratio) and presented the full results set: “We found a three-way interaction effect of genotype, session, and prehension accuracy (Supplemental Table 2K; Supplemental Figure 4), with genotype effects for both accuracies on the naive session and successful prehensions during the learning session (Supplemental Table 2L-N), and accuracy effects in control mice across the learning and training sessions (Supplemental Table 2O-P). This indicates that Mα2 cell activity might selectively refine the neural signal balance during planning/execution phases of motor execution particularly on initial training sessions.”

(3) While the authors have improved their statistical reporting, key information is still missing in several places. For example, no N-numbers are listed in legends for figure 3, and there is no mention of the number of mice for analysis in figures 2 and 3. For clarity, the authors should also include the statistical test performed in the figure legends for any p-values shown in the figure.

We thank the reviewer for the attention to details, and clarified that Figure 2 shows latency analysis for the same dataset as Figure 1, we now explicitly state the number of mice and assemblies in Figure 3 results section, and added the statistical tests performed in each panel’s legend.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this revision the authors address some of the points, but they also make some technical errors. My overall view of the manuscript hasn't changed since the original evaluation.

Previously I noted that SC sparsity presents an issue when comparing to full FC matrices. They author misinterpreted the Honey et al paper. They resampled ALL entries of the SC matrix (including zeros) from a Gaussian distribution. In effect, this assigns zeros small (but uniform) weights. In Honey et al., the authors resampled only existing edge weights from a gaussian distribution (the rationale at the time was that there might be pushback against the extremely heavy-tailed edge weight distribution). In other words, the zeros are still zeros following this resampling procedure.

That said, I agree that the log transform is likely useful or necessary given edge weight distributions.

In short, I still think that the approach is interesting and meritorious, I just don't think the execution is correct.

Thank you very much for pointing this out. Regarding Gaussian resampling, we recalculated the results to avoid including zeros of the SC matrix in the resampling. As before, we confirmed that when the ROI count is small (200 or less), Gaussian resampling tended to produce a higher SC-FC correlation (Extended Data Figure 2-2a), as the ROI count increased so too did the Sparsity Rate (Extended Data Figure 2-2b), and the log transform tended to produce a higher SC-FC correlation (Extended Data Figure 2-2a). However, for both methods we still observed a tendency for the FC-SC correlation to decrease as the ROI count increased. Therefore, we will continue to use the log transform, but we will update Ext.Data.Fig.2-2 and now explicitly state in the text (lines 132-137) that there is a tendency for FC-SC correlation to be higher as the Sparsity Rate increases.

Reviewer #3 (Public review):

Summary:

In this manuscript, Okuno et al. re-analyze whole-brain imaging data collected in another paper (Brezovec et al., 2024) in the context of the two currently available Drosophila connectome datasets: the partial "FlyEM" (hemibrain) dataset (Scheffer et al., 2020) and the whole-brain "FlyWire" dataset (Dorkenwald et al., 2024). They apply existing fMRI signal processing algorithms to the fly imaging data and compute function-structure correlations across a variety of post-processing parameters (noise reduction methods, ROI size), demonstrating an inverse relationship between ROI size and FC-SC correlation. The authors go on to look at structural connectivity amongst more polarized or less polarized neurons, and suggest that stronger FC-SC correlations are driven by more polarized neurons.

Strengths:

(1) The result that larger mesoscale ROIs have higher correlation with structural data is interesting. This has been previously discussed in Drosophila in Turner et al., 2021, but here it is quantified more extensively.

(2) The quantification of neuron polarization (PPSSI) as applied to these structural data is a promising approach for quantifying differences in spatial synapse distribution. The revision now uses morphological cable length for some analyses rather than straight-line distance, which improves the realism and interpretability of these results.

Weaknesses:

One should not score noise/nuisance removal methods solely by their impact on FC-SC correlation values, because we do not know a priori that direct structural connections correspond with strong functional correlations. In fact, work in C. elegans, where we have access to both a connectome and neuron-resolution functional data, suggests that this relationship is weak (Yemini et al., 2021; Randi et al., 2023). Similarly, I don't think it's appropriate to tune the confidence scores on the EM datasets using FC-SC correlations as an output metric. While it is likely that some FC-SC relationship does exist at large scales, it does not in my view justify use of this metric for evaluating noise removal methods, since such methods may inadvertently remove real neural correlates. This concern remains unaddressed in the revision.

Thank you for pointing this out. Firstly, regarding C. elegans, and mentioned in our Discussion section, the FC of calcium dynamics in the soma was compared with the SC of the whole cell in C. elegans studies (Yemini et al., 2021; Randi et al., 2023). Neurons in C. elegans are non-spiking, and calcium dynamics have been shown to differ between compartments (soma and other parts) in a neuron (Hendricks, et al., 2012). While fly and human studies compared the SC and FC of synaptic population dynamics in brain regions, C. elegans studies compared the SC of cells (not regions) with the FC of dynamics in the cell body. This discrepancy is thought to explain the differing results.

In support of our approach, numerous studies (cited in our manuscript Introduction) have demonstrated statistically significant FC-SC relationships across species and modalities, including human rs-fMRI and diffusion MRI, marmoset retrograde tracing and rs-fMRI, and Drosophila calcium imaging and connectomics. These findings suggest that still SC provides an important anatomical constraint on FC.

We also used FC-SC detection in addition to FC-SC correlation. Correlation measures similarity by normalizing the covariance between FC and SC values by the product of their standard deviations. On the other hand, FC-SC detection measures the detection accuracy (AUC) of FC. Since FC and log-transformed SC are fundamentally different, both correlation and detection are considered useful indicators. In both indicators, high correlation and high AUC were observed using the same nuisance removal method. Our results suggested that head movement and the attenuation of fluorescent molecules due to long-duration imaging are the sources of noise, and this provides supporting evidence that the procedure may be improving signal quality. Therefore, we consider FC-SC correspondence to be a biologically motivated validation metric for nuisance removal and a way to validate nuisance removal factors.

However, we agree that FC-SC correspondence may not be regarded as a ground truth objective, and that biologically meaningful functional relationships may also arise through indirect pathways, network effects, neuromodulation, and other mechanisms not captured by direct SC. As examples, neuropeptides diffuse to transmit signals, while gap junctions tightly and directly connect neurons, and there is also a pathway mediated by glia. Although SC cannot be equated with FC, we believe that the relationship between the two remains strong. To investigate this matter further, we consider it necessary to conduct additional research involving the simultaneous measurement of whole-brain FC (calcium) and ‘non-synaptic’ signals.

We have rewritten the manuscript to say that SC is not a ground truth but a biologically motivated evaluation metric (line 102) for nuisance removal, and we have added content to the discussion around the points discussed here (lines 296-306).

Any discussion of FC-SC comparisons should include an analysis of excitatory/inhibitory neurotransmitters, which are available in the fly connectome dataset. The authors examine the ratios of input and output neurotransmitters in different defined regions. However, I think it would be more useful to integrate the neurotransmitter information more fully into the assessment of SC, for instance: examining the signed weight (excitatory - inhibitory), or by examining the excitatory and inhibitory networks separately.

Thank you for suggesting the idea. This matter has not been thoroughly investigated in this study. Figure 3g shows the correlation between neurotransmitters (rate of neurons) and FC-SC correlation, but we have not been able to analyze the effects on FC-SC in detail. Due to this, we think that this topic requires further analysis as part of future work.

Comparisons between fly and human MRI data are also premature here. Firstly, the fly connectomes, which are derived from neuron-scale EM reconstructions, are a qualitatively different kind of data from human connectomes, which are derived from DSI imaging of large-scale tracts. Likewise, calcium data and fMRI data are very different functional data acquisition methods-the fact that similar processing steps can be used on time-series data does not make them surprisingly similar, and does not in my view constitute evidence of "similar design concepts."

We are not saying we have presented evidence; we are merely saying that it is possible that it is a similar design concept. That is, the fundamental calculation is performed analog through local addition, subtraction, and multiplication by multiple synapses, and when it is necessary to transmit the data over a distance, it is converted to digital by convolution. This is the idea of an analogue-digital-hybrid circuit (Shirahata et al., Euro. J. Neurosci., 2025). Although C. elegans lacks sodium channels and most of neurons are non-spiking, AWA cell has been shown to exhibit action potential mediated by calcium spikes (Liu et al., Cell, 2018). This suggests that even C. elegans utilize an analog-digital-hybrid circuit. ‘FC’ is correlation between local activity of synapses, and FC-SC showed a high correlation between regions. This result was similar in both flies and mammals. In other words, functions are implemented locally (analog) and connected over a wide area (digitally). We believe this design is common across multiple species, even at different brain size scales. To address your concern, we modified the text on line 320 to give a more conservative tone.

The comparison of FlyEM/FlyWire connectomes concludes that differences are more likely a result of data processing than of inter-individual variability. If this is the case, the title should not claim that the manuscript covers individual variability.

The analysis of the wedge-AVLP neuron strikes me as highly speculative, given that the alignment precision between the connectome and the functional data is around 5 microns (Brezovec* et al, PNAS 2024).

Thank you for pointing that out. We have changed the title because the original title was considered too broad and general.

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) I still feel that the title and introduction overstate the results, despite the small changes to the introduction.

Thank you for pointing that out. We have changed the title because the original title was considered too broad and general.

(2) Re: the use of a custom FC-SC score in this manuscript, I agree with the authors that the overall approach is common. However, I would like to see some evidence that the qualitative conclusions in the paper are robust to the way this score has been designed, particularly because it deviates from metrics used in prior work.

In relation to this, we also performed an additional analysis of the FC-SC correlation using the Gaussian resampling method (Honey et al., 2009) [6]. Compared to the log transform of the SC matrix, Gaussian resampling showed a higher correlation when the ROI count was 200 or less, and as the ROI count increased and the Sparsity Rate rose, the log transform showed a higher correlation (Ext.Data.Fig.2-2a and b). However, in both methods we still observed a tendency for the FC-SC correlation to decrease as the ROI count increased. This content has been added to the main text (lines 132-137).

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

The authors have substantially strengthened the manuscript in response to my comments. In particular, they have improved the treatment of non-canonical calls, added further illustrative examples at the level of individual RNA variants, repeated pathway enrichment using an appropriate expression-matched background, assessed treatment-associated cell viability, and moderated several biological claims. The revised manuscript is now most compelling as a technical benchmarking and best-practice resource for high-confidence prediction of a common RNA chemical modification from nanopore direct RNA sequencing.

The matched-input comparison of two methods, use of unmodified RNA controls, and inhibitor treatment are important strengths. Together, these experiments provide solid support for the central conclusion that careful filtering and appropriate controls can substantially reduce likely false-positive calls and yield a reproducible set of high-confidence predictions. The added analyses also provide useful illustrations of the capacity of long-read sequencing to assign predictions to individual RNA variants, although they do not establish broad superiority over the short-read comparison method.

A few claims remain insufficiently supported. First, the discussion of non-DRACH sites should cite Cancer mutations rewire the RNA methylation specificity of METTL3-METTL14 (Science Advances, DOI: 10.1126/sciadv.ads4750). In particular, Figure 3C of that study shows that the normal METTL3-METTL14 enzyme retains measurable activity on non-DRACH substrates; this provides a useful precedent for describing the inhibitor-sensitive GGAUU calls as plausible candidates rather than treating non-DRACH calls, especially those detected only by GLORI, as presumptively artefactual. The revised manuscript appropriately notes technical and biological explanations for non-canonical calls and identifies the GGAUU sites as candidates requiring further validation, but this additional context would improve interpretation.

We thank the reviewer for reminding us of this interesting publication. We have included the citation and adjusted our discussion accordingly (lines 576-579).

Second, the comparison between Dorado and GLORI remains overinterpreted. The matched-input design and inhibitor perturbation are important strengths, but the current analysis does not establish that sites detected only by GLORI are false positives or that Dorado is a reference standard. This would require, for example, direct comparison of inhibitor responsiveness among GLORI-only and shared sites, while accounting for coverage, conversion efficiency, and other method-specific biases; therefore, phrases such as "GLORI exhibits reduced specificity," "largely spurious," and "validated by an orthogonal approach" are not fully supported by the data presented.

Thank you for this comment. We agree that our original language potentially overinterpreted the GLORI-Dorado comparison. In our GLORI dataset, the relatively high gene-level non-conversion rate (>5%) particularly limits interpretation of low-proportion sites. Although this background has little effect at high m⁶A/A proportions, it can substantially affect calls in the 10-20% range. Consistent with this limitation, GLORI-only sites were predominantly low-stoichiometry and more often occurred outside DRACH motifs, whereas shared sites were enriched at higher predicted m⁶ A/A proportions. GLORI coverage was similar between categories, and all sites analyzed were STM2457-responsive. However, residual non-conversion may disproportionately affect low-fraction calls. Thus, our findings do not establish that GLORI-only sites are false positives but instead indicate unresolved method-specific differences. We have adjusted the section accordingly (lines 327-382) and added two additional subplots in Fig. S21 (lines 1193-1202 contain the new figure legends).

Similarly, the thresholding approach should not be described as "unbiased." The analysis is useful and empirically informed, but it relies on selected parameters, a manually specified penalty, and predetermined decision criteria. Describing the procedure as "data-driven" or "empirically calibrated against matched unmodified RNA controls" would more accurately convey both its value and its limitations.

Thank you for this comment. We agree that this language should be used carefully. To our knowledge, we have already refined the relevant wording in the current revised version.

The additional RNA-variant examples are helpful, but they demonstrate an advantage of long-read data rather than broadly proving that Dorado "outperforms" GLORI for RNA-variant-level quantification. A more accurate formulation would be: "Direct RNA sequencing provides RNA-variant-resolved predictions that are not readily assignable using short-read GLORI data, as illustrated at several loci."

We have revised the wording to emphasize that DRS enables RNA-variant-resolved predictions that are not readily assignable using short-read GLORI data (lines 384-385 and 404-406).

Finally, the authors now acknowledge that the functional significance of cell-type differences remains unresolved, but the abstract still presents the results as evidence of "finely tuned" regulation, and the discussion links them to neuronal function. The data provide solid evidence for differences in predicted modification proportions between cell types, but the evidence is incomplete for claims about functional consequences; these statements should therefore be framed as context or hypotheses for future study rather than as inferences from the present experiments.

Thank you for this comment. In the revised manuscript, we do not describe the observed cell-type differences as evidence of “finely tuned” regulation or infer functional consequences for neuronal function. Any potential relevance is framed only as context for future investigation. We refer to lines 43-46 and 602-606, where we describe our observations about increased m⁶A/A site ratios in HD10.6 cells compared to NHDFs.

Reviewer #2 (Public review):

The revised manuscript has improved substantially. The authors have addressed the main concerns raised during the previous round by introducing an IVT-based calibration framework, evaluating background calls across probability thresholds, examining base calling mismatches, and replacing "stoichiometry" with the more appropriate term "predicted modification proportion." The expanded discussion of non-DRACH predictions is also useful and appropriately balanced. Overall, the study now provides a valuable practical framework for Dorado-based RNA modification analysis.

I have only a few remaining comments, all of which should be addressable through clarification and minor textual revisions.

(1) The comparison between NHDF and HD10.6 cells does not appear to include independent biological replicates. The observed differences in predicted m6A/A proportions should therefore be presented as differences between the two datasets rather than as general cell-type-specific effects. The interpretation is already cautious in the Discussion, but similar wording should be used in the Abstract, Results heading, and title if applicable.

We thank the reviewer for this suggestion and agree that the wording should avoid overinterpretation. We consider the title appropriate, as the manuscript reports differences in predicted m⁶ A proportions between fibroblast and neuronal datasets. However, to ensure greater precision, we revised the relevant sentence in the Abstract (lines 43-46) and two Results section headings (lines 130-131 and 408-409).

(2) The direction of the comparison in Figure 3D should be clarified. The percentages represent the fraction of GLORI sites that is also detected by Dorado. Thus, the analysis shows that Dorado increasingly recovers high-proportion GLORI sites. It does not directly demonstrate that high-proportion Dorado predictions are increasingly validated by GLORI. The text should reflect this distinction, and the figure should clearly identify which circle represents each method.

We thank the reviewer for this clarification. We revised the text in lines 367-369 to clarify that Dorado increasingly recovers high-proportion GLORI sites, and we adjusted Fig. 3D to improve clarity.

(3) The ratio of calls detected in IVT relative to biological samples is a useful empirical measure of background, but it is not formally a false-positive rate because the true status and testability of every site are not known. A term such as "IVT-to-sample call ratio" or "empirical background-call ratio" would be more precise and would not alter the main conclusion regarding the value of stringent filtering.

The reviewer’s point is well taken, and we have replaced the use of false-positive with ‘background signal’ throughout the manuscript when dealing with our approach and results. We have however retained the use of false-positive as a term when directly quoting from other published studies (regardless of whether they used this term correctly).

(4) The description of the change-point framework still contains the placeholder "at least X-fold more signal." The actual enrichment threshold should be provided. The authors should also ensure that a log2 ratio threshold of 1.5 is not described as 1.5-fold enrichment, since these values are not equivalent.

We thank the reviewer for catching this. We have corrected the sentence on lines 739-740 to note that the fold enrichment is 1.5-fold which equates to a log2 ratio threshold of ~0.585.

These are relatively minor issues. The authors have responded constructively to the previous reviews, and I do not consider further experimental work necessary.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Add the Science Advances reference, DOI: 10.1126/sciadv. ads4750, to the discussion of non-DRACH sites and use it to contextualize inhibitor-sensitive GGAUU sites as plausible candidates requiring independent validation.

(2) Revise language implying that GLORI-only sites are false positives, that GLORI has reduced specificity, or that Dorado serves as the validating reference method; instead, describe the observed agreement and acknowledge unresolved method-specific differences.

(3) If feasible, compare inhibitor responsiveness directly among shared and GLORI-only sites, reporting coverage and conversion-related quality measures for those categories.

(4) Replace "unbiased" thresholding language with "data-driven" or "empirically calibrated against matched unmodified RNA controls."

(5) Revise broad "outperforms" language about RNA-variant-level quantification to specify that long-read sequencing enables predictions at individual RNA variants in the illustrated examples.

(6) Remove or further qualify statements that infer finely tuned regulation or neuronal functional effects from differences in predicted modification proportions alone.

We have addressed these recommendations as described above.

Author response:

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

eLife Assessment:

This study reports the relative importance of Tie1 and Tie2 signaling for atrial versus ventricular trabeculation. It is an important study and is one of the few works to date that have carefully and simultaneously analyzed these two processes. In line with a previous study in zebrafish, the authors demonstrate key differences between atrial and ventricular trabeculation. While the imaging and quantitative data were conducted with solid and validated methodology throughout the manuscript, the work would benefit from more rigourous approaches where Tie1/2 signaling is disrupted prior to the onset of atrial/ventricular trabeculation, to allow for a more direct comparison.

We thank the editors for the eLife assessment. We would like to request that the following statement be modified: “…the work would benefit from more rigourous approaches where Tie1/2 signaling is disrupted prior to the onset of atrial/ventricular trabeculation, to allow for a more direct comparison”. We request this change for the following reasons:

We utilized two distinct genetic mouse models in this study (as summarized in Fig. 7I), comprising conventional knockouts (Tie1^tm1a/tm1a, Tie1^ΔICD/ΔICD and Tie1^ΔICD/ΔICD;Tek^+/-) and inducible gene deletion models (Tek^iECKO, Tie1ICD^iECKO, and Tie1ICD^iECKO;Tek^+/-) [1-3].

The Tie1^tm1a/tm1a line is equivalent to the previously published Tie1^-/- mouse line as demonstrated in our prior work and by others [1, 4-6]. For the Tie1^ΔICD/ΔICD line, as described in the previous report [2], the expression level of Tie1^ΔICD decreased dramatically compared with that of wild-type mice, which may result from the nonsense-mediated mRNA decay. Based on the lymphatic and venous phenotypes [1, 2], we conclude that the Tie1^ΔICD/ΔICD line is almost equivalent to Tie1 null mice.

Therefore, the Tie1 or Tek alleles were inactivated prior to the onset of atrial and ventricular trabeculations, as shown in Fig. 1, Fig. 2, Fig. 3, Fig. 5A-D, and Supplemental Fig. 3. Based on these findings, we propose that TIE1 is differentially required for atria versus ventricle morphogenesis, and acts synergistically with TIE2 during cardiac trabeculation.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Ding et al. use genetic mouse models to demonstrate that atrial trabeculation is more dependent on Tie1/Tie2 signaling than ventricular trabeculation. With additional experimentation that would support the current claims, the results may hold significant value, as atrial trabeculation remains an understudied phenomenon in cardiac biology with potential implications for atrial cardiomyopathy and atrial fibrillation.

Strengths:

Detailed characterization of atrial versus ventricular trabeculation across different developmental time-points, and the use of appropriate animal models to address the scientific question at hand.

Weaknesses:

The authors have consistently treated mice with tamoxifen after ventricular, but not atrial, trabeculation has already started. As such, the observed cardiac phenotypes - where predominantly atrial trabeculation is affected - might be a mere consequence of the precise time window in which Tie1/2 signaling was impaired, rather than a direct measurement of its relative importance for atrial versus ventricular trabeculation. The conclusions of the paper may thus be significantly strengthened by depleting Tie1/2 signaling prior to the onset of ventricular trabeculation, as is done for atrial trabeculation.

We thank the reviewer for the comments.

Regarding the timeline of gene deletion and tamoxifen treatment, we would like to provide the following clarification.

Fig. 1-3: As described in the Methods and Materials, Tie1^tm1a/tm1a is a knockout first mouse model established from EUCOMM embryonic stem cells (EPD0735-3B07) targeting Tie1 gene. Therefore, the Tie1^tm1a/tm1a line is equivalent to the previously published Tie1 null mice (Tie1^-/-). The Tie1^Flox/Flox mouse line (with exon 8 floxed) was generated when the lacZ reporter and neo-cassette were excised using the FLPeR mice.

Fig. 5A-D: To investigate the synergy of TIE1 and TIE2 in cardiac trabeculation, we utilized the Tek^+/- and Tie1^ΔICD/+ mouse lines and they were crossbred to generate double mutant mice harboring a homozygous Tie1 mutation and a single null Tek allele (Tie1^ΔICD/ΔICD;Tek^+/-). Although no obvious defects were observed in atrial or ventricular structures following Tie1 deficiency alone at E10.5, both atrial and ventricular development were disrupted in Tie1^ΔICD/ΔICD;Tek^+/- mutants at the same stage (Fig. 5A-D).

Supplemental Fig. 3: To verify the role of TIE1 in atrial development, we employed alternative knockout mouse line targeting the Tie1 intracellular domain by floxing exons 15 and exon 16 (Tie1ICD^Flox/Flox). Mutants harboring these null alleles are designated as Tie1^{ΔICD/ ΔICD}. As detailed in the previous publication, the line is also equivalent to the previously published Tie1 null mice (Tie1^-/-). The cardiac phenotypes shown in Supplemental Fig. 3 are indeed similar to those of Tie1^tm1a/tm1a mutant mice.

For the inducible knockouts targeting Tie1, Tek and both, the results are shown in Fig. 4, Fig. 5E-H, Fig. 6, and Fig. 7.

Fig. 4: As mice homozygous for Tek mutation (Tek^-/-) die before E10.5 [3, 7], we performed studies using the inducible knockout line targeting Tek (Tek^Flox/-;Cdh5-Cre^ERT2 named as Tek^iECKO), as shown in Fig. 4.

Fig. 5-7: To investigate the synergy of TIE1 and TIE2 in the cardiac trabeculation at the later stages of embryogenesis (Fig. 5E-H, Fig. 6) and the postnatal stage (Fig. 7), we used the inducible knockout models targeting Tie1/Tek, including Tie1ICD^iECKO (Tie1ICD^Flox/-;Cdh5-Cre^ERT2) and Tie1ICD^iECKO;Tek^+/- (Tie1ICD^Flox/-;Cdh5-Cre^ERT2;Tek^+/-).

Reviewer #2 (Public review):

Summary:

Ding et al. examine the role of TIE1 in cardiac chamber morphogenesis using genetic mouse models targeting Tie1, Tek, or both, and analyzing endocardial cell-mediated chamber formation across multiple embryonic developmental and postnatal stages, supported by analysis of published single-cell datasets and new bulk RNA seq analyses of murine cardiac tissue. The authors find that Tie1 and Tek expression is higher in atrial than ventricular endocardial cells. Notably, endothelial Tie1 is required for atrial trabeculation at E12.5, but is less critical in ventricular trabeculation. TIE1 also acts synergistically with TIE2 during atrial trabeculation. While Tie1 deficiency alone does not cause defects at E10.5, combined heterozygous deletion of Tek disrupts both atrial and ventricular development at E10.5. This synergy is further supported by analyses at later embryonic stages and in postnatal hearts.

Strengths:

The study is well-designed, clearly written, and supported by high-quality figures. The performed experiments demonstrate a previously unrecognized role for Tie1 in cardiac development and identify synergistic control of cardiac morphogenesis by Tie1 and Tie2. This synergy is consistent with the previously identified roles of Tie1 and Tek in venous development and with Tie1 involvement in angiopoietin-dependent postnatal vascular and lymphatic remodeling. Together, these findings support a role for Tie1 as a contributor to Ang1-Tie2 signaling during heart development.

Weaknesses:

The manuscript does not include direct mechanistic studies; however, RNA seq analysis of atria and ventricles showed reduced expression of Tek, Dll1, and Notch1 upon Tie1 deficiency in developing hearts. Although previously reported mechanisms, such as TIE1-TIE2 heterodimer formation and effects on endothelial junctions, migration, or survival are discussed, no direct mechanistic experiments are performed. Addressing some of these mechanisms would have clarified the basis of Tie1-Tie2 synergy. As two distinct Tie1 models are used, including one targeting the kinase domain, the authors should state whether phenotypes differed or were similar between models.

We thank the reviewer for this comment. In this study, we provide genetic evidence that TIE1 is differentially required for atrial versus ventricular trabeculation. Although the precise molecular mechanisms underlying TIE1 function warrant further investigation, we have provided compelling genetic evidence of its synergistic role with TIE2 during this process. Crucially, the two genetic models targeting Tie1 (Tie1^tm1a/tm1a, Tie1^ΔICD/ΔICD) produced consistent cardiac and vascular phenotypes, as shown in both this study and our previous work [1, 2].

Regarding endocardial TIE1 in atrial morphogenesis, fully elucidating its downstream mechanism may require the isolation of primary endocardial cells for further study. However, our previous work using HUVECs have demonstrated that TIE1 acts synergistically with its homologue TIE2 to regulate AKT-mediated COUP-TFII protein stability [1, 3]. The essential roles of COUP-TFII in venous and atrial development have been well-documented in the literature [8, 9]. We have expanded our Discussion section to reflect these mechanistic insights.

Reviewer #3 (Public review):

Summary:

Ding et al. investigate the roles of TIE1 and TEK (Tie2) in mouse cardiac development, with a particular focus on atrial trabeculation. The authors employ multiple genetic models, including Tie1ICDflox/flox (with Cdh5-CreERT2), a knockout-first allele (EUCOMM, Tie1 tm1a/tm1a), and a Tek deletion model.

Based on the dataset from Feng et al. 2022 Nat Commun, the authors report increased expression of Tie1 and Tek transcripts in atrial endocardial cells compared to ventricular cells at embryonic day (E) 14.5. Loss of Tie1 leads to early atrial trabeculation defects detectable at E12.5, whereas ventricular defects appear later and are less pronounced at E14.5. Chamber-specific RNA sequencing reveals stronger transcriptional changes in atrial tissue.

Conditional deletion of Tek results in a similar phenotype, with more pronounced atrial defects. Combined deletion of Tie1 and Tek (Tie1 ΔICD/ΔICD; Tek+/-) leads to earlier and more severe defects in both atrial and ventricular trabeculation and results in embryonic lethality around E12.5, suggesting a synergistic interaction between the two genes.

Conditional endothelial deletion of Tie1 combined with heterozygous global Tek at later embryonic stages allows analysis at later time points and again shows more severe defects in atrial trabeculation. Postnatal analysis of this model reveals reduced heart-to-body weight ratios and potential mild atrial abnormalities.

Strengths:

(1) The authors address chamber-specific signaling mechanisms underlying atrial versus ventricular trabeculation, an area of high developmental and clinical relevance.

(2) The study provides a comprehensive temporal analysis across multiple embryonic stages.

(3) The use of multiple genetic models strengthens the overall conclusions and allows comparative interpretation.

(4) While focusing on trabeculation, the authors also include observations on coronary vessel development, increasing the broader relevance of the work. The findings are therefore of interest to the wider cardiovascular research community.

Weaknesses:

(1) Timing of recombination vs. trabeculation onset

Ventricular trabeculation begins earlier than atrial trabeculation. Since tamoxifen (in contrast to 4-hydroxytamoxifen) requires metabolic activation, Cre-mediated recombination will occur with a delay. This suggests that atrial trabeculation may be targeted before its onset, whereas ventricular trabeculation may already be underway for 2-3 days at the time of effective gene deletion.

How do the authors account for this discrepancy in their interpretation?

Have earlier induction time points been tested to better capture the onset of ventricular trabeculation? This limitation should be explicitly discussed.

(2) Clarity of genetic models and experimental design

The study employs several genetic constructs. It would improve clarity if, for each experiment, the specific genetic model and tamoxifen regimen were clearly described before presenting the results.

We thank the reviewer for the detailed and constructive comments. As detailed above, for studies employing the inducible gene deletion mouse models (models (Tek^iECKO, Tie1ICD^iECKO, and Tie1ICD^iECKO;Tek^+/-), the genetic models and tamoxifen treatment schemes have been provided in the related figures.

For the investigation of TIE1 or TIE2 in atria versus ventricle morphogenesis at earlier embryonic stages, we utilized the conventional knockouts targeting Tie1 (Tie1^tm1a/tm1a, Tie1^ΔICD/ΔICD) or the combined deletion of Tie1 and Tek (Tie1^ΔICD/ΔICD;Tek^+/-), as detailed above.

(3) Tie1 tm1a/tm1a phenotype vs. known global knockout

Previous studies (PMID: 8846781, 7596437) show that complete Tie1 loss leads to severe edema, vascular rupture, and embryonic lethality around E13.5-E14.5.

How does the Tie1 tm1a/tm1a allele differ, given that animals appear to survive longer? Is this allele hypomorphic rather than a full knockout?

This point requires clarification.

Tie1^tm1a/tm1a is equivalent to the full Tie1 knockout (Tie1^-/-). As demonstrated in our prior work, the Tie1^ΔICD/ΔICD model produced lymphatic and blood vascular phenotypes similar to those of Tie1^-/- mutants [1, 2, 5, 6].

(4) Limited mechanistic insight

While the authors aim to investigate underlying mechanisms, the current study is largely descriptive and based on mRNA expression and genetic interaction analyses (Tie1/Tek co-deletion). Direct mechanistic insights into signaling pathways remain limited. However, the dataset provides a valuable foundation for future mechanistic studies, which should be more clearly acknowledged in the discussion.

We thank the reviewer for the comment. We have incorporated this discussion into the revised manuscript

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The conclusions of the paper may be significantly strengthened by addressing several of the following comments:

Major critiques:

The authors state that Angpt1 is more prominently expressed in atrial versus ventricular myocardium and that this might explain the larger impact of Tie1 deletion on atrial versus ventricular trabeculation. However, other ligands for Tie1/Tie2 have been described, such as Svep1, Angpt2, and Lect2. It would be great if the authors could show the relative expression of these ligands in atrial versus ventricular cardiomyocytes over time.

We appreciate the reviewer's valuable suggestion. To address this, we analyzed the scRNA-seq dataset to compare the expression profiles of key ligands (Angpt1, Angpt2, Svep1, and Lect2) between atrial and ventricular cardiac cells during embryonic development. These new data have been integrated into Supplemental Fig. 1F. Our analysis reveals that Angpt1 is differentially enriched in atrial cells relative to ventricular cells. However, no distinct inter-chamber differences were detected for Svep1 or Angpt2. Notably, Lect2 transcripts were virtually absent in both chambers; this is fully congruent with our bulk RNA-seq data, which showed no detectable Lect2 expression in whole-heart lysates.

Likewise, the authors indicate that ANGPT1-TIE2 signaling is stronger in atria than ventricles at E14.5. Could this reflect a temporal rather than spatial difference? How does ANGPT1-TIE2 signaling compare between atria and ventricles during different steps of the trabeculation process?

We thank the reviewer for this insightful question regarding spatial versus temporal dynamics. To address whether the observed differences reflect a temporal shift or a sustained spatial pattern, we evaluated Angpt1 expression across a developmental timeline spanning the major stages of trabeculation, from initiation through remodeling (E10.5 to E18.5).

As shown in the newly added Supplemental Fig. 1F, Angpt1 is consistently and differentially enriched in atrial cells relative to ventricular cells throughout all examined embryonic stages. This sustained divergence confirms that elevated ANGPT1-TIE2 signaling in the atria is a distinct spatial feature rather than a transient temporal shift. This finding aligns with our ligand-receptor interactome analysis between cardiomyocytes and endocardial cells (Supplemental Fig. 1E). Furthermore, a specialized role for ANGPT1-mediated signaling in atrial morphogenesis has been independently demonstrated by Kim et al. (Cell Rep, 2018), supporting our model that this pathway is uniquely critical for the assembly of the atrial muscular network [10].

Ding and colleagues demonstrate that loss of endothelial/endocardial Tie1 results in absent atrial trabeculae, while ventricular trabeculae are only moderately impacted. As ventricular trabeculation is initiated much earlier than atrial trabeculation, this discrepancy might, however, be secondary to the precise time point within trabecular network formation at which Tie1 was deleted. The make sure that Tie1 does not prevent ventricular trabeculation to an equal extent as atrial trabeculation, the authors should conduct additional experiments in which Tie1 is deleted before the onset of ventricular trabeculation (i.e., E8.5). Consistent with this, Tie1 knockout mice display substantial ventricular trabeculation defects (Figure 5). This comment extends to the analysis of the Tie2 knockout mice, where knocking out Tie2 starting from E12.5 does not affect ventricular trabeculation at E14.5 but impairs ventricular trabeculation when hearts are analyzed later (at E17.5). Additionally, Figure 5 clearly demonstrates that ventricular trabeculation is impacted in the combined absence of Tie1 and Tie2. Overall, a more detailed analysis of the relative importance of Tie1/Tie2 signaling for atrial versus ventricular trabeculation with more appropriate tamoxifen regimens needs to be performed to support the claims made by the authors.

While one can deduce from the Methods section that tamoxifen was administered at E10-5-E11.5 for the results depicted in Figure 1, no information is provided regarding the tamoxifen regimens for the following figures, obscuring proper interpretation of the results. The authors should clearly state the precise time window in which they depleted endothelial Tie1 for each Figure in both text and legends, as this essential information is missing in Figures 2 and 3.

We thank the reviewer for pointing this out. To rigorously investigate the differential requirement of TIE1, as well as its synergy with TIE2, during the distinct stages of atria versus ventricle trabeculation, we utilized both conventional (constitutive) and inducible gene knockout models. For the inducible genetic models, the exact timelines of gene deletion and tamoxifen treatments are detailed within their respective figure panels and legends. Below is a brief overview of the constitutive null models used in this study.

Fig. 1-3 (constitutive null models): As described in the Materials and Methods, the Tie1^tm1a/tm1a line is a “knockout-first” mouse model generated from EUCOMM embryonic stem cells (EPD0735-3B07) targeting Tie1 gene. Consequently, the Tie1^tm1a/tm1a line is functionally equivalent to previously published Tie1 null mice (Tie1^-/-). The Tie1^Flox/Flox mouse line (harboring a floxed exon 8) was generated by excising the lacZ reporter and neo-cassette using FLPeR delete mice. As described above, the Tie1^ΔICD/ΔICD line is also equivalent to Tie1 null mice.

Fig. 5A-D: To investigate the genetic synergy between TIE1 and TIE2 during the initiation phase of cardiac trabeculation, we crossbred Tek^+/- and Tie1^ΔICD/+ lines to generate compound mutants harboring a homozygous Tie1 mutation paired with a single null Tek allele (Tie1^ΔICD/ΔICD;Tek^+/-). While Tie1 deficiency alone yielded no obvious defects in atrial or ventricular structures at E10.5, compound Tie1^ΔICD/ΔICD;Tek^+/- mutants exhibited severe disruption in both atrial and ventricular development at the same developmental stage (Fig. 5A-D).

In the last paragraph, Ding et al. propose a model in which Tie1/Tie2 signaling drives atrial versus ventricular endothelial/endocardial specification. To substantiate this claim, the authors should identify several genes that differentiate between these two and demonstrate that their asymmetric expression pattern is perturbed in Tie1/2 mutant embryos. Alternatively, single-cell RNA-seq in control and Tie1/2 mutant embryos could provide a more holistic view of endothelial specification processes and their impact on myocardial shape and function.

We thank the reviewer for these constructive suggestions. We agree that a comprehensive single-cell RNA-seq analysis of Tie1/Tek mutant embryos would provide a holistic view of endocardial specification. While performing this extensive sequencing is beyond the scope of our current study, we believe our present combination of chamber-specific bulk RNA-seq and functional genetic models provides a strong foundation for these mechanisms. Further studies are certainly warranted to provide deeper single-cell insights in this direction, and we have added this point to our revised Discussion section.

A recent publication (Albu et al., Nature Communications) found no evidence for Nrg/Erbb and Notch signaling in atrial trabeculation, but reported that YAP signaling was implicated in the latter. This raises important questions: Did the authors observe Yap-mediated signaling in their RNAseq datasets? Could Yap/Taz be investigated in control and Tie1/2 mutant mice? Is there a link between Tie1/2 and Yap/Taz signaling in other systems, such as venous versus arterial endothelial specification?

We thank the reviewer for this insightful comment. Based on our bulk RNA-seq data, we did not observe an obvious change in Yap1 and Wwtr1 (Taz) transcript expression in the hearts of Tie1 null mice compared to their littermate controls. However, this transcriptomic data does not exclude the possibility of post-translational regulation occurring at the protein level, such as alterations in protein phosphorylation, nuclear translocation, or the activation of downstream YAP/TAZ target genes. We agree that investigating potential alterations in YAP signaling following the induced endothelial deletion of Tek or compound Tie1/2 represents an important direction for future study.

In contrast to the study by Albu and colleagues, the manuscript presented here observes Notch1 downregulation in the atria but not ventricles (Figures 3F, G). What could be the reason for these discrepancies? Does loss of Tie1 and/or Tie2 impair Nrg1, VEGF, or is Notch signaling more impactful in atria versus ventricles at the protein levels?

We thank the reviewer for the insightful comment. Using a Zebrofish model, Albu et al., (Nat Comm 2024) [11] reported no evidence for Nrg/ErbB or Notch signaling in atrial muscle network formation. Based on our bulk RNA-seq analysis of heart tissues from Tie1 deficient mice compared to littermate controls, we demonstrated a decrease in Erg1 and Notch1 transcripts in Tie1 mutants. In contrast, we detected an increase in Vegfa transcript levels, which may result from compensatory changes in cardiac angiogenesis induced by hypoxic stress upon TIE1 deficiency. The biological significance of these transcriptomic changes requires further investigation. We have modified the text to include this discussion in the revised manuscript.

In Figures 5 and 6, it is not clear which genotype was used as a control. Are these controls Tek+/-, Tie1ICDECKO, or WT mice? If there were any differences between these genotypes, these should be reported with the appropriate statistical tests.

We thank the reviewer for pointing this out. We have added the information in the revised manuscript. Related to Fig. 5 and Fig. 6, the genotype for the control mice used are described in the Methods and Materials section. The genotypes of the Tie1/Tek knockout and control mice are as follows: Tie1ICD^Flox/-;Cdh5-Cre^ERT2 named as Tie1ICD^iECKO, littermates Tie1ICD^Flox/+ or Tie1ICD^Flox/+;Cdh5-Cre^ERT2 mice named as Control. Tek^Flox/-;Cdh5-Cre^ERT2 named as Tek^iECKO, littermates Tek^Flox/+ or Tek^Flox/+;Cdh5-Cre^ERT2 mice named as Control. Tie1ICD^Flox/-;Cdh5-Cre^ERT2;Tek^+/- named as Tie1ICD^iECKO;Tek^+/-, littermates Tie1ICD^Flox/+;Cdh5-Cre^ERT2;Tek^+/-, Tie1ICD^Flox/+;Tek^+/-, Tie1ICD^Flox/+;Cdh5-Cre^ERT2;Tek^+/+ or Tie1ICD^Flox/+;Tek^+/+ named as Control.

Minor points:

The resolution of the retinal stainings should be improved.

We thank the reviewer for pointing this out. We performed the analysis of retinal vascular phenotype in this study, which is for the verification of gene deletion efficiency.

Sarcomeric defects have been observed in tie1-/- zebrafish. Can the authors check if such sarcomeric defects are also present in their mouse models and if they are more pronounced in atrial versus ventricular cardiomyocytes?

We thank the reviewer for the interesting comment. We have not studied whether there is any sarcomeric defect in Tie1 null mice, which requires further investigation.

If Tie1/2 signaling is more critical for atrial than ventricular development and function, is there any evidence for an association between atrial cardiomyopathy and/or atrial fibrillation in humans carrying pathogenic Tie1/Tie2 mutations?

We thank the reviewer for this insightful comment. Whether human patients carrying pathogenic Tie1/Tie2 mutations have atrial cardiomyopathy and/or atrial fibrillation warrants further investigation.

Bulk RNAseq reveals that Tie1tm1a/tm1a mice have reduced Nrg1 mRNA levels in the heart (Figure 2I), but this is not reflected in the atrial or ventricular transcriptomics (Figure 3). Could the authors explain this discrepancy in more detail?

We thank the reviewer for pointing this out. As described above, there was a decrease of Nrg1 transcript level in hearts of Tie1 mutant compared to that of the littermate controls. The biological significance of this change requires further investigation. We have included this discussion in the revised manuscript.

Reviewer #3 (Recommendations for the authors):

Unfortunately, line numbers are not provided, which makes it difficult to refer to specific passages.

We thank the reviewer for pointing this out. We have added line numbers to the revised manuscript t.

While it is appropriate to mention in the Discussion that Tie1 variants have been associated with lymphatic defects, this information should be removed from the abstract, as the manuscript does not address lymphatic biology, and this statement distracts from the main focus of the study.

We thank the reviewer for the comment. In the abstract background, we stated: “…TIE1 variants or loss of function mutations were reported in a subset of lymphedema patients, and it is unknown whether the patients have also cardiac defects in addition to the lymphatic abnormality.” By framing the introduction this way, we aimed to establish the central question of our study: whether Tie1 variants or loss-of-function mutations lead to cardiac abnormalities, which could ultimately contribute to or exacerbate systemic lymphedema alongside primary lymphatic defects.

Figure 5F should include single-channel images for Tie1 staining to allow proper assessment of signal specificity and localization.

We thank the reviewer for this comment. The co-staining of TIE1 and PECAM1 is intended primarily to demonstrate gene deletion efficiency. As shown In Fig. 5F, TIE1 is efficiently deleted in Tie1ICD^iECKO;Tek^+/- mice compared to control mice. Furthermore, as previously reported by Cao et al. [1] and Shen et al. [2], the mutant mice (Tie1ICD^iECKO;Tek^+/-) exhibit disrupted venous development alongside defective lymphatic formation.

Parts of the manuscript use non-scientific language, for example, "doubly knockout mice" or "atria appear to have some wavy edges." These should be revised for a more formal scientific tone.

We thank the reviewer to point this out. We have modified the text in the revised manuscript.

Typo error in Figure 1D: "ventricle"

We thank the reviewer to point this out. We have made the correction with Fig. 1D.

Reference

(1) Cao, X., et al., Endothelial TIE1 Restricts Angiogenic Sprouting to Coordinate Vein Assembly in Synergy With Its Homologue TIE2. Arterioscler Thromb Vasc Biol, 2023. 43(8): p. e323-e338.

(2) Shen, B., et al., Genetic dissection of tie pathway in mouse lymphatic maturation and valve development. Arterioscler Thromb Vasc Biol, 2014. 34(6): p. 1221-30.

(3) Chu, M. et al., Angiopoietin receptor Tie2 is required for vein specification and maintenance via regulating COUP-TFII. Elife, 2016. 5:e21032.

(4) Rodewald, H.R. and T.N. Sato, Tie1, a receptor tyrosine kinase essential for vascular endothelial cell integrity, is not critical for the development of hematopoietic cells. Oncogene, 1996. 12(2): p. 397-404.

(5) D'Amico, G. et al., Loss of endothelial Tie1 receptor impairs lymphatic vessel development-brief report. Arterioscler Thromb Vasc Biol, 2010. 30(2): p. 207-9.

(6) Qu, X., et al., Abnormal embryonic lymphatic vessel development in Tie1 hypomorphic mice. Development, 2010. 137(8): p. 1285-95.

(7) Dumont, D.J., et al., Dominant-negative and targeted null mutations in the endothelial receptor tyrosine kinase, tek, reveal a critical role in vasculogenesis of the embryo. Genes Dev, 1994. 8(16): p. 1897-909.

(8) You, L.R., et al., Suppression of Notch signalling by the COUP-TFII transcription factor regulates vein identity. Nature, 2005. 435(7038): p. 98-104.

(9) Wu, S.P., et al., Atrial identity is determined by a COUP-TFII regulatory network. Dev Cell, 2013. 25(4): p. 417-26.

(10) Kim, K.H., et al., Myocardial Angiopoietin-1 Controls Atrial Chamber Morphogenesis by Spatiotemporal Degradation of Cardiac Jelly. Cell Rep, 2018. 23(8): p. 2455-2466.

(11) Albu, M., et al., Distinct mechanisms regulate ventricular and atrial chamber wall formation. Nat Commun, 2024. 15(1): p. 8159.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

There is prior literature showing a robust relationship between sulcal interruptions in the posterior occipital temporal sulcus (pOTS) and reading ability. The goals of this study were to extend these findings to children examined longitudinally as they become better readers, and to examine the underlying white matter properties in individuals with and without pOTS sulcal interruptions. To do this, the authors collected longitudinal structural, diffusion, and behavioral data in 51 children (TP1 age 5.5, TP3 age 8.2 years).

First, the authors found that the gyral gap was consistent across time within the subject. This is expected, as they state in the introduction that sulcal patterns are typically established in utero. Next, they found that children with an interrupted pOTS have higher reading scores (across a variety of measures) at timepoint (TP) 3 than children with continuous pOTS, and this was specific to the pOTS, as no associations emerged for the anterior OTS or MFS; this is again expected from prior literature. They then found that the binary presence of this gap, but not anterior OTS or MFS predicted T3 reading performance. Further, they found that a subsample of the lowest readers at TP1 did not have differences in reading score by gyral gap, but that this difference emerged at TP3. Additionally, the gyral gap at TP1 is similar to variance TOWRE 3 reading skills as some behavioral measures at TP1. Examining underlying white matter in a smaller subset of children, the authors found higher MD in children with an interrupted pOTS vs. those with a continuous pOTS, which was contrary to their hypothesis, and higher local connectivity for interrupted, aligning with their hypothesis, but this difference was no longer present when accounting for TP3 reading scores. The authors conclude that structural properties, in this case, the gyral gap, may guide neural plasticity for reading.

Strengths:

This paper has an interesting set of longitudinal data to examine the perhaps changing relationship between sulcal interruptions in the pOTS with reading scores. I commend the authors on data collection and attention to detail in the anatomical analyses.

Weaknesses:

However, my enthusiasm was somewhat dampened after finding numerous prior publications on this very topic and I'm unclear as to how much more this paper adds to the current literature. Would we expect the existence of sulcal interruptions to be aligned with reading skills in older kids but not younger kids? Is the point to see if the interruptions exist prior to reading (but these children are not really prereaders)? What is the alternative- why would these interruptions not exist? After all, this anatomy is determined prenatally. Children who have pOTS interruptions at T1 should also have these interruptions at T3 (and indeed that is what the authors find). So how can this be the mechanism that drives plasticity? The authors also talk about the neuronal recycling hypothesis but their data cannot speak to this because they do not have fMRI data nor does their sample include only prereaders with no reading experience. The conclusions are overall overstated and not supported by the results. I think this paper could add interesting knowledge for the specific subfield of reading and the brain. However, the current state of the results, especially with the inclusion of so many trending results and the comparison of so many different processing pipelines and models, in addition to a conclusion that is not motivated by the work makes it difficult to appreciate the paper.

We thank Reviewer 1 for their detailed feedback. The reviewer raises several related concerns regarding the novelty and framing of the study, the interpretation of stable sulcal anatomy, early reading abilities, statistical robustness, and the proposed link between pOTS morphology, white matter, and reading development. In response, we have revised the manuscript to make clearer that the main contribution is not the stability of pOTS morphology itself, nor simply the replication of previously reported cross-sectional associations with reading, but rather how this stable anatomical feature relates prospectively to reading acquisition from the onset of literacy instruction. In particular, we now make more explicit that left pOTS interruption contributes to later reading beyond associations already present at age 5, including through an updated serial mediation analysis, and we better highlight how this relationship develops over time.

The reviewer’s comments also prompted us to explain more clearly how the complementary analyses in the full sample and in the subgroup with very limited initial reading skills converge to support our conclusion that left pOTS interruption is a particularly strong longitudinal predictor of later reading relative to the benchmark behavioral and familial predictors considered, despite the collinearity between pOTS interruption and emerging literacy skills at T1. We have renamed this subgroup more accurately from “pre-readers” to “initial minimal readers” and clarified its characteristics and range of reading abilities.

We also moved key analyses from the Supplement to Figure 3 to make the distinction between separate and unique longitudinal contributions easier to follow. The initial-minimal-reader analyses provide a complementary assessment in which confounding with early reading is substantially reduced. At the same time, as the reviewer accurately pointed out, some of our previous wording implied a more categorical superiority than the analyses warrant; we have therefore softened these claims throughout the manuscript while preserving the conclusion that pOTS interruption is among the strongest longitudinal contributors considered. We also added, in response to Reviewer 2, a new systematic analysis supporting the relative cognitive specificity of the pOTS effect.

Finally, we made several interpretations more precise, notably by presenting the white-matter findings as a candidate pathway rather than a definitive mechanism and by removing implications that our data directly test the neuronal recycling hypothesis. We believe these revisions make the longitudinal contribution, scope, and significance of the findings considerably clearer, and we are grateful to the reviewer for prompting these improvements.

Reviewer #2 (Public review):

Summary:

This manuscript examined the impact of sulcal morphology on reading development. A very specific feature on the ventral surface of the brain was identified, namely the presence of an interruption in the posterior portion of the left occipitotemporal sulcus (pOTS). Compared to children with a continuous pOTS, children with an interruption at age 5 years had better reading ability at age 8. This was a large effect measured in 43 children. Surprisingly, this morphological feature was a better predictor of reading ability than measures of pre-literacy cognitive skills, such as phonological awareness. The effect was tested and reproduced across several different measures of reading ability. The authors hypothesised that the mechanism underlying this benefit related to greater local connectivity, which confers a computational advantage. This was demonstrated using analysis of diffusion-weighted imaging data in 29 of the children obtained at age 8.

Strengths:

The novelty of the manuscript is threefold: (i) the measure was made in children who were pre-literate (previous work was in older children and adults); (ii) longitudinal brain imaging and behavioural data were analysed; and (iii) diffusion data were analysed to test a hypothesis about the underlying mechanism.

The manuscript is exceptionally well written. The methods are detailed and easily reproduced. The approach is thoughtful and meticulous. All possible alternatives appear to have been considered. Where possible, further analyses have been done to address these alternatives. For example, the testing of the specificity of the sulcal interruption to left pOTS was an important addition. None predicted reading skills.

Weaknesses:

The correlation of the interruption with all kinds of literacy measures and in particular reading comprehension and then PIQ suggest this interruption might confer a more general cognitive advantage rather than specifically a reading one.

It would be interesting to know if the anatomical difference predicts any other cognitive ability or if there might be any cognitive cost (a negative correlation) of this sulcal interruption.

The location of the interruption in the sulcus is quite variable and in some cases, there is more than one interruption. The sample size is probably not big enough to compare these different patterns or to evaluate the influence of the location of the sulcal interruption.

The sample is quite high-functioning and the generalisability of the findings outside of this specific population is inevitably limited.

We would like to thank Reviewer 2 for their positive feedback and for their insightful suggestions.

Cognitive specificity: We agree with the reviewer that the association between left pOTS interruption and performance IQ, as measured in the concept formation learning task, on top of its association with multiple measures of literacy, raises the possibility that this sulcal feature relates to general cognition more broadly. The fact that reading and general cognitive abilities are highly correlated and mutually influence one another over development complicates any attempt to interpret the effect of left pOTS interruption as purely reading-specific. Our results however support a relative specificity of this sulcal feature to reading: left pOTS interruption remains a strong longitudinal predictor of later reading, even when controlling for the moderate association with performance IQ, and its impact on reading skills is larger than on pIQ. Importantly, a new systematic analysis of associations with all the cognitive and academic skills obtained at T3 further supports a relative cognitive specificity to reading: We show that while left pOTS interruption is also significantly associated with several assessments of math, language and general cognition at age 8 (possibly due to the inherent correlations across these domains), hierarchical clustering indicates that pOTS interruption aligns most closely with literacy-related outcomes (cf. See rev 2 recommendation comment (1)). We observe no cognitive costs of left pOTS interruption across the many linguistic, pre-literacy and cognitive domains tested.

Neuroanatomical precision: We also fully agree that our sulcal marker of interest, i.e., whether the posterior portion of the left pOTS is interrupted or not, is relatively coarse and may lack in neuroanatomical precision (though this robustness may alternatively be seen as a strength). Beyond this first approximation, several questions remain unanswered, including whether additional interruptions confer an additional reading advantage, or whether interruptions in more specific locations of the left posterior OTS would be optimal. Unfortunately, multiple interruptions were too rare and gap locations too unevenly distributed in our cohort to support adequately powered comparisons. These questions can only be answered on larger sample sizes, which we now mention in our revised Discussion. Please refer to See rev 2 recommendation comment (3) for more details and for the results of tentative explorations which did not support clear trends.

Sample limitations: The characteristics of our sample (being both from a high socio-economic background, as often seen in pediatric research, and high-functioning) indeed limit the generalizability of our results, as we now acknowledge in the Discussion. However, we replicate results by Cachia and colleagues (2018) which were obtained in a sample where half of the participants were from a rural and (very) low socio-economic background, in order to match a sample of illiterate adults, and this association has been now found in multiple samples with various SES and cognitive characteristics. This suggests that overall such associations may be generalizable across extremely varied socio-economic backgrounds and also possibly along the spectrum of general cognitive skills (cf. R2 comment-toaddress #5).

Additional correction made during revision:

During the revision process, we identified one subject for whom an anterior OTS gap had been incorrectly included in the diffusion analyses (participant 6007 on previous Supplementary Figure S6). We removed this gap, reran all diffusion analyses, and updated the relevant results and figures. The results and conclusions remained essentially unchanged.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comment (1) The results are currently framed in a manner that makes it difficult to figure out what the main findings of the paper are, and to see if those findings support their conclusions.

The beginning of the results is focused on showing that the longitudinal pipeline has a better consistency across time points, yet the authors still report follow-up analyses with the cross-sectional pipeline, even though those results are only trending. I think it would make more sense to only focus on the longitudinal pipeline because that is the novelty of this manuscript.

We fully agree with Reviewer 1 that the longitudinal pipeline shows better consistency and likely constitutes a more accurate, less noisy measure of sulcal interruptions, as we report. For this reason, all the results reported in the main figures concern the longitudinally processed data only.

Yet, we choose to also include and report supplementary cross-sectional analyses since these analyses, while less reliable, are important for several conceptual reasons:

(1) Since we wanted to demonstrate that T1 brain anatomy predicted T3 behavior longitudinally, it seemed important as a proof of principle to show that this prediction held with T3 brain data completely unseen, i.e., with T1 cross-sectional processing only. We have now clarified the text referring to this analysis (lines 192-196):

“This importantly implies that left pOTS morphology at T1 was still a significant longitudinal predictor of T3 reading behavior when T3 brain images were not used to improve T1 anatomical segmentations, i.e., with T1 cross-sectional processing alone, despite noisier tissue segmentations with cross-sectional processing (see also Reuter et al., 2012).”

(2) Since most studies are cross-sectional, reporting cross-sectional effects may constitute a more relevant reference for other studies, and for the generalizability of our results.

(3) Larger samples were available for the cross-sectional processing, allowing to test a maximum number of children, despite the higher noise in the sulcal measurements.

Please also note that across the 4 types of processing (2 timepoints x cross-sectional & longitudinal pipelines), only pOTS interruptions measured cross-sectionally at T3 showed a marginal association with reading scores, while the other 3 processings showed a large significant effect. Having established that cross-sectional measures are less reliable, and since our main goal was to demonstrate that T1 morphology predicted T3 reading, such trending results are found in the least reliable and least relevant condition, with otherwise large and significant effects, which seems quite acceptable. If anything, we believe that transparently reporting these consistent results altogether support, rather than challenge, the robustness of the association.

Our main findings are summarized in the last paragraph of the Introduction as well as in the first paragraph of our Discussion.

Comment (2) Also, as the authors note, it is known that sulcal patterns develop in utero; therefore, we would expect a perfect alignment between TP1 and TP3- there should be a more in-depth analysis of the lack of alignment in the main results. And further, this is more reason that the results should focus on the longitudinal pipeline which is closer to that expectation. However, it is unclear whether T1 data processed through the longitudinal pipeline preserves anatomical nuances of that time point (since the images are averaged across the timepoints). Maybe the cross-sectional pipeline is a better depiction of how anatomy changes as a child develops.

We thank Reviewer 1 for raising these relevant questions.

First, we would like to clarify that T1 longitudinal processing does preserve anatomical nuances of this time point. In fact, the averaging of T1 and T3 MRIs into a subject base is only an intermediate step of the longitudinal pipeline, which then crucially allows to re-initialize T1 MRI and T3 MRI tissue segmentations separately from their respective scans, but using this time the common tissue priors provided by the subject base (hence the reference to distinct “T1 longitudinal” and “T3 longitudinal” processing). We describe this in the Methods (lines 764-769):

“When images were available at both Time 1 and Time 3 for a child (N=43), the longitudinal Freesurfer pipeline was used, which first creates an unbiased subject average across time points (“base”) and then restarts multiple processing steps at each time point separately from the base template in order to refine tissue segmentations on each image (respectively T1 and T3 longitudinally processed images, Reuter et al., 2012; see Figure 1A).”

Therefore, a perfect match between T1 and T3 anatomy is not expected, even if we could expect (and indeed find) pOTS morphology, and interruption patterns in particular, to be extremely stable. Actually, our left pOTS interruption classification only changes between the T1 and T3 longitudinal processing for one child, with two left pOTS sulcal components separated by a distance estimated as 1.34mm at T1 and 0.99mm at T3, leading to a different classification given our 1 mm minimum-distance interruption criterion. We added the following sentence accordingly (lines 146-149):

“Only one child changed left pOTS interruption classification between T1 and T3 under longitudinal processing, due to the measured inter-component distance crossing the predefined 1-mm threshold, consistent with high stability of this macro-anatomical feature.”

Our results are therefore consistent with the view that sulcal interruption patterns are set in utero and stable after birth. Given that there actually is limited direct evidence to this effect, we chose to confirm this stability as a first step, which we refer to in the Discussion (lines 606-610):

“In our study, we observed high reliability of the pOTS interruption from age 5 (T1) to age 8 (T3), which is consistent with the longitudinal stability of interruptions of (i) the intraparietal sulcus and postcentral sulcus (Schwizer Ashkenazi et al., 2024), (ii) sulci in inferior frontal cortex (Tissier et al., 2018), and (iii) patterns of the anterior cingulate sulcus (Cachia et al., 2016) observed in late childhood (approximately 8 years onwards) to early adulthood.”

As discussed above, the longitudinal processing pipeline leads to better precision in assessing neuroanatomy, as well as its change across time (see the seminal paper by Reuter et al., 2012), which is why we mostly use measures derived from the longitudinal processing.

Comment (3) The analyses starting on p.4 ("Left pOTS interruption is prospectively associated with better reading skills") seem overly fixated on cross-sectional vs. longitudinal processing pipelines. The key comparisons should be on anatomical specificity (posterior or anterior OTS, etc) as well as including T1 reading skills as a regressor to see if the interruptions at T1 explain additional variance in T3 skills.

We thank Reviewer 1 for highlighting that we had started our result paragraph by a verification that was less essential. We have now reordered our results to highlight those concerning the anatomical specificity to the left pOTS, in the analyses reported under “The association between left pOTS interruption and reading skills was robust to different measurements of reading skills and sulcal interruption in four ways” (line 175 onward).

Testing whether the interruptions at T1 explain additional variance in T3 skills over and above T1 reading skills is so essential that it is actually the object of the entire next subsection “The effect of left pOTS interruption on reading accumulates over time” (lines 235-274). This claim is supported by the following findings:

(1) In the subsample of minimal readers with little to no reading experience at T1, we see that despite the absence of associations between left pOTS interruptions and reading at T1, the association is present and significant at T2 and T3 and appears to grow (lines 243-253 and Supplementary Figure 4);

(2) In the serial mediation analysis across the whole sample that follows, we observe important and significant additional contributions of left pOTS on later reading skills beyond the contributions at T1. We have now clarified this essential point and rephrased these results, notably adding this particular sentence:

“Importantly, there were also significant contributions of left pOTS interruption onto T3 reading on top of those mediated through T1, with large cumulative effects through T2 and directly onto T3 (d*c+f: ꞵ = 4.580, SE = 1.757, p = .009), while indirect effect through T1 TOWRE scores alone were non-significant (a*b*c+a*e: ꞵ = 0.971, SE = 0.839, p = .25).” '

We thank the reviewer for bringing to our attention that this was lacking in the previous version and needed to be made explicit. (Please note that p-values for the serial mediation analysis slightly changed, as the bootstrap was rerun to estimate this additional path.)

The analyses in the following section “Left pOTS interruption makes a strong longitudinal contribution relative to established predictors of reading” also support the same conclusion that left pOTS interruptions explain variance in T3 reading over and above T1 reading, despite the concern of collinearity with early literacy skills in our entire sample, as we explain below in details.

Comment (4) The authors do a version of this on p. 6 lines 269-273 and show that indeed, pOTS binary classification contributes a very similar proportion of the variance in T3 reading scores as the next best predictor (letter knowledge). They do not seem to be significantly different- are they?

When longitudinal contributions are tested separately, left pOTS interruption accounts for 20.5% of T3 reading variance while T1 letter knowledge accounts for 19.6% of this variance. While these values appear numerically close, one should first bear in mind that, as an emerging literacy measure rather than a pre-literacy predictor from a different domain, letter knowledge is expected to be a strong predictor of future literacy skills. The fact that left pOTS interruption, a much less proximal neuroanatomical marker, explains slightly more variance in reading stands out as a more interesting observation.

More importantly, while proportions of explained variance cannot be compared statistically in a straightforward fashion, the collinearity between these two predictors across the full sample anyway completely biases this comparison: because left pOTS interruption already accounts for significant variance in letter knowledge (cf. Figure 3B and analyses reported in lines 320-326), the estimation of the longitudinal contributions of letter knowledge to reading skills is inflated by this collinearity, picking up in addition some of the true effects of sulcal interruption on T3 reading (and vice versa).

For that reason, our claim that left pOTS interruption is a strong longitudinal predictor of reading relative to pre-literacy skills actually rests on the integration of all of the results reported in the corresponding section (lines 275-367), including: the contributions of each predictor separately under discussion, in addition also their unique contributions above all other predictors, and the analysis of the underlying collinearity and how it reduces the power in testing the true effects of pOTS interruption, as well as the same analyses repeated in the subsample of minimal initial readers where the collinearity between pOTS and emerging literacy is removed. (Please note that in this subsample, letter knowledge has minimal nonsignificant contributions to T3 reading, contrarily to sulcal interruptions - cf. Figure 3D and F and Comment-to-address #6).

To clarify this entire section and how all these results converge to support our conclusion, we have now moved several supplementary figure panels from Supplementary Figure 5 to Figure 3 (also addressing See rev 2 recommendation comment (9)) and largely edited the text, including:

“These significant associations between left pOTS interruption, performance IQ and pre-literacy skills (Figure 3B and D), as well as potential associations between pre-literacy skills themselves (cf. correlation matrices in Supplementary Figure 5D and H), make it challenging to fairly assess the separate unique contributions of each of these variables to the longitudinal prediction of reading skills. For instance, because left pOTS interruption explains a significant amount of variance at T1 in letter knowledge, early TOWRE scores and performance IQ, some of its true direct effect on future T3 reading skills is already captured in a baseline model including these cognitive predictors only, even before left pOTS interruption is explicitly entered as a predictor. Yet, even when controlling in a such a stringent way for all pre-literacy skills, early reading abilities, family history of dyslexia and their shared variance with left pOTS interruption in such nested model comparison, left pOTS interruption still had a marginal additional contribution to predicting T3 TOWRE reading scores (ΔR² = 5.0%, F(1, 31) = 3.74, p = .062) inspite of this important collinearity. Rapid naming and family history were the only two other predictors that outperformed left pOTS interruption in terms of unique contributions to T3 reading (ΔR² = 7.7% and 6.6% for RAN and mother ARHQ respectively, see Figure 3C), possibly because these predictors were among the least confounded with others (see Figure S5D for correlations among predictors) and thus among the least affected by collinearity. Letter knowledge, in contrast, had the smallest, non-significant unique contributions to T3 reading (ΔR² = 0.61%, p = .50).”

Thus, while the separate contributions of letter knowledge to T3 reading was almost as large as that of left pOTS interruption, their unique contributions above each other and other predictors strikingly differed: ΔR² = 5.0% for left pOTS interruption vs. 0.61% for letter knowledge.

Please also note that our statistical approach is particularly stringent: our nested model comparisons evaluated the unique contributions of each variable above all other predictors, i.e. after accounting for the variance in the outcome jointly explained by the covariance between predictors. In such cases of highly collinear variables, statistical power is importantly reduced.

Comment (5) And again even if the T1 presence of pOTS interruption explains this additional variance, what does that tell us? The brain (as measured by this pOTS measure) does not change from T1 to T3, as evidenced by this result: Lines 178-180: "left pOTS morphology at T1 remained a significant longitudinal predictor of T3 reading without taking into account brain information at T3, i.e., with T1 cross-sectional processing alone." T3 anatomical data is therefore redundant to this fit. This is further confirmed by the results in lines 220-226, showing differences in T1 TOWRE scores between children with continuous vs. interrupted pOTS. Additilly, the finding that "the effect of pOTS interruption accumulates over time" may instead suggest that TOWRE skills are more accurately measured at T3, especially for the lowest scores. It had alreaonady been shown that pOTS interruptions correlate with reading skills in readers- paired with assessment issues/lack of norms at T1 of these reading measures and the lack of change in pOTS over time, these results are not surprising.

We fully agree with the reviewer that given the previously observed associations between left OTS interruptions and reading skills in 10-year-olds and adults (Borst et al., 2016; Cachia et al., 2018) and the general understanding that sulcal patterns are stable after birth, it was natural to expect that left OTS patterns observed before or at the onset of literacy acquisition would predict future reading skills. Yet, validating hypotheses -however natural they may seem- is essential for moving science forward.

Beyond this expected longitudinal association, the fact that left pOTS interruption at T1 predicts additional variance in T3 reading above early literacy skills and all other cognitive, linguistic and familial predictors of literacy also tells us new and important things. Notably:

(1) It shows that this sulcal marker is a large and important predictor of future reading skills, with a predictive performance comparable to or exceeding the conservative benchmark of pre-literacy skills and familial predictors used for the identification of children at risk of dyslexia. This highlights the relevance of this neuroanatomical marker at a theoretical level for reading acquisition, with possible practical implications for early identification and intervention further down the line.

(2) We learn that the association between left pOTS morphology and reading is not merely a byproduct of pre-existing associations between sulcal morphology and cognitive or familial factors before literacy learning. Instead, our results clarify the neurocognitive origins of the relationship between reading and OTS morphology by showing a prospective and sustained association with reading acquisition between sulcal morphology and reading acquisition during literacy learning.

Concerning the relevance of T1 vs. T3 brain data, please refer to our response to Comment-to-address #2, in which we clarify that the longitudinal pipeline serves to improve the reliability of the assessment of sulcal interruptions at T1, but that our results are indeed also confirmed using only T1 brain data.

Concerning the matter of measurement accuracy of the TOWRE at T1, we agree that reading is harder to measure at the very beginning of literacy acquisition, and that the TOWRE is not normed below age 6. For this reason, our analyses controlled for early literacy skills at T1 using both scores of letter knowledge, as measured by the age-appropriate and normed WMRT letter identification subtest, and the principal component of the two TOWRE raw scores (scaled). This ensured a strict control procedure for all measurable emerging literacy skills: letter knowledge, but also word reading and phonological decoding (if already acquired in precocious/early readers, or to confirm this was not acquired yet).

In the absence of TOWRE norms for all children at T1, we used this TOWRE principal component to derive a T1 TOWRE population-scaled index. This scaling mostly served to ensure that this early reading score would be of a similar nature and scale as the T2 and T3 TOWRE standard scores, notably for statistical and plotting purposes (Supplementary Figure 4A and D).

Interestingly, we observed in the full longitudinal sample that left pOTS interruption was already associated around age 5 with this T1 TOWRE score, in addition to the letter identification scores. In the context of stronger associations observed at T2 and T3, this suggests that the T1 TOWRE score, even if not normed nor very accurate, does still capture relevant variance in early literacy skills.

Comment (6) Further, while one main conclusion is that the gyral gap predicts T3 reading ability better than typical behavioral TP1 measures (but it really does not appear to), this result is mixed in with a series of nonsignificant results (labeled as marginal or trending, but p>0.05) and difficult to parse sections. Some, but not all, analyses are performed in a set of 'pre-readers' (defined as scoring <95th percentile on a reading test which is not particularly stringent), and at some points, the authors get a significant result in the whole sample, but not the prereaders and interpret these results as only trending because of a smaller sample size (line 287), but at other times they get a trending result in the main group, and a significant result in the pre-reader group (line 303), and choose to focus on the result of the prereaders. This inconsistency makes me skeptical of why some analyses were done with different samples. The definition of a pre-reader is not really a pre-reader but rather just below an average reader. This also leads back to my question above on the underlying hypotheses, which critically needs to focus on prereaders. Can you further explain the decision to run some analysis in pre-readers (example line 285/286) and further explain what it means to be a pre-reader in this sample? Perhaps try to think of a more direct way to examine the impact of the gyral gap at TP1 predicting behavioral performance at TP3, as a trending result in the whole sample followed by significance in just a subset is not convincing (line 298, 303).

We thank Reviewer 1 for this opportunity to clarify our results and some misunderstandings.

We acknowledge, and are sorry for, the lack of clarity of our previous explanations, especially as some analyses are complex and some conclusions require integrating results across multiple analyses to understand the overall implications. We believe that our statistical approach was justified, though perhaps not well explained in the original version. We have now clarified and addressed these issues in the revision by renaming pre-readers to ‘minimal initial readers’ - which is indeed more accurate (thank you for raising this concern) -, better explaining the composition of this subsample and what analyses restricted to this subsample bring (notably lines 243-253, and in the descriptive demographic Table 1), rewriting the entire section “Left pOTS interruption Left pOTS interruption makes a strong longitudinal contribution relative to established predictors of reading” (lines 275-367), and adding a number of figure panels to Figure 3 (previously in supplementary figure 5), to aid the comparison and integration of results across both samples to support our conclusion. To answer directly the reviewer’s questions and remarks:

Why two groups? We carry out analyses both in our entire available sample and in a subsample with little to no early literacy skills, since these samples are both relevant for our hypotheses and offer different advantages:

The entire sample allows to maximize sample size, and is more representative of the general population. This naturally implies that some kindergarteners have emerging literacy skills, including letter knowledge, knowledge of a few sight words and minimal decoding. Interestingly, we found these early literacy measures to already be significantly associated with our sulcal marker, but two problems also derive from this: (1) These emerging reading skills preclude from directly testing in this sample our strong hypothesis that pOTS interruption before literary learning predicts future reading scores. (2) The collinearity between the T1 behavioral predictors and left pOTS interruption is a statistical obstacle to testing reliably how each predictor truly contributes to predicting future reading skills separately (as explained in our answer to Reviewer 1’s Comment-to-address #4 above, taking the comparison with letter knowledge as a key example).

To remove the association between pOTS and T1 reading and bypass both these problems, we perform additional analyses in a decently-sized subsample of children with little to no reading abilities at T1 - that we have now renamed more accurately as ‘initial minimal readers’.

Definition and composition of our subsample of “initial minimal readers”:

Kindergarteners are expected to know letters and how to write their names, they may have understood the basics of the alphabetic principle and phonological decoding, and may have learned to recognize a few highly frequent sight words through repeated exposure in their books and environments (e.g., “the”, “and”). From our entire sample, including a number of children accordingly able to read some sight words and decode some syllables and pseudowords (cf. Table 1), we defined a subsample of lowest readers by using a cut-off of a TOWRE population-scaled index at T1 under 95 (due to the lack of norms, cf. see rev 1 recommendation comment (5)). For reference, the equivalent standard score of 95 would correspond to a 37th percentile in a normal distribution.

This cut-off was chosen as it translated to very little actual reading abilities overall and crucially removed the statistical association between pOTS and T1 reading needed to address our two problems, while being still decently sized to allow for our statistics (n = 24, i.e. 56% of the sample, cf. distributions on Supplementary Figure 4A). We now specify more clearly notably in the results lines 244-253:

“We conducted a supplementary analysis in the subset of 24 children with the lowest reading scores at T1 (defined as those with a TOWRE T1 population-derived composite score equivalent below 95). Hereafter, we refer to these children as initial minimal readers: 79% could not decode a single syllable or pseudoword in 45 s, with a maximum of four pseudowords decoded, and 63% could not recognize a single frequent sight word, with a maximum of seven words recognized. Although these children showed no difference in T1 reading scores as a function of whether their left pOTS was interrupted or continuous (F(1, 19) = 0.21, p =.66, ΔR² = 0.82%, Cohen’s d = 0.034), [...] “

and methods - lines 988-991:

“We therefore selected a subsample of children whose TOWRE standard score equivalent at Time 1 was below 95, resulting in a subset of 24 initial pre-readers (median of 0 words read in 45s in SWE, range: 0-7; median of 0 syllables in 45s in PDE, range: 0-4; see Table 1).” as well as Table 1.”

Expecting a larger proportion of children of this age with no word reading or decoding at all would be both unnecessary for our analyses and developmentally unrealistic, especially in this high-SES sample, selecting an atypical population at especially high risk of dyslexia.

Discrepancies between statistics in the full sample and the subsample:

Because this subsample was chosen to remove the associations at T1 between pOTS and early literacy which affected some analyses (cf. Comment #4), some discrepancies in the results across the two samples are actually expected. Conducting statistics on 56% of the full sample may also affect the statistical power for other analyses in the subsample.

First, concerning issue #1 of the simple longitudinal prediction of T2 and T3 reading, we find that left pOTS interruption also reliably predicts future reading in the subsample of initial minimal readers, even if the association is absent at age 5, confirming analyses in the main sample.

Concerning the issue #2 of the comparison with other benchmark predictors of literacy, our results in the entire sample show that despite a large amount of collinearity between our T1 predictors (documented, explained and quantified in lines 320-334, Figure 3B and Supplementary Figure 5D, including strong significant associations of left pOTS morphology with T1 reading, T1 letter knowledge and T1 performance IQ) and despite using the most stringent statistical approach to control for it (nested model comparison), left pOTS interruption still has a marginal contribution to predicting T3 reading on top of all other early literacy, pre-literacy, cognitive and familial predictors of reading (Figure 3C), in line with its large separate contributions (Figure 3A). In the subsample of initial minimal readers, where there is only partial collinearity with performance IQ but not early literacy, we find the specific longitudinal contributions of left pOTS morphology to be strong and significant over and above all of the other T1 behavioral and familial predictors (see Figure 3F and corresponding text). In other words, the collinearity present in the full sample weakens statistical power when controlling for other collinear predictors, with only marginal unique longitudinal pOTS contributions in our stringent analyses, while removing this collinearity in the subsample reveals a large and highly significant unique contribution, in line with the large contributions of pOTS observed overall (Figure 3A, D, and F).We believe that detailing these analyses and finding coherent results on both samples, with potential differences in statistical strength explained by specific factors, overall brings reliability to our results and conclusions, rather than challenges them.

The reviewer refers also to one interesting incidental finding when examining the T1 cognitive associations of the pOTS interruption in the full sample, consisting in a significant association with the concept formation subtest, measuring a form of performance IQ (though a weaker association than with reading skills, see Figure 3B). When restricting to the subsample of initial minimal readers, this association was then indeed found marginal, though of a similar amplitude as in the full sample. We therefore speculated that the combination of a significant effect in the full sample, and of a marginal finding in the subsample, revealed a possibly true underlying effect, while likely affected by a decrease of statistical power associated with using only 56% of the sample. This effect and speculation are in no way fundamental to our study and claims. The new additional analysis revealing a significant association with performance IQ at T3 again in the full sample (Supplementary Figure 6) would however further support this idea.

Comment (7) Given that there are these potentially major differences in the pOTS, how are the results of structural connectivity mapped to a common template for Figure 4? There is likely an error in registration at the exact location of the observed differences.

Individual structural connectivity results were mapped to an MNI template space using standard procedures (lines 919-922 of our Methods:):

“The obtained individual probabilistic fiber density maps were then transformed into template MNI space for statistical analysis using non-linear registration in ANTs, from individual diffusion space (individual FA map) to the HCP1065 MNI FA template, and smoothed with a 4-mm-FWHM Gaussian kernel.”

As the reviewer points out, group analyses performed in atlas space are inherently affected by variations in neuroanatomy across individuals and by the quality of registrations. Mapping individual connectivity results to template space was however the only approach that made sense to us to evaluate which connectivity benefits would be associated with the presence of such gaps, given the variability in the number and location of gyral gaps in children with interrupted sulci, and the need to find a common comparison ground with children who had a continuous sulcus. High neuroanatomical variability around the pOTS in particular likely plays against us in investigating such connectivity differences. In spite of these difficulties, we do find differences that seem to explain the reading advantage associated with the presence of gyral gaps.

Comment (8) While I appreciate the control analyses for the white matter connectivity, I think more robust analyses are more appropriate. Are there MD differences between white matter underneath sulci and gyri of neighboring or even distant regions? I'm not sure what the white matter analyses are really adding to the story. The white matter differences do not explain the differences in T3 reading ability.

Our rationale for choosing and conducting the reported white matter analyses was the following: Having provided strong evidence that left pOTS sulcal interruptions facilitate reading acquisition, a naturally following question was that of its underlying mechanisms. It had been hypothesized - though never tested directly - that white-matter differences associated with the presence of gyral gaps may improve the connectivity around sulcal interruptions and constitute a potential mechanism linking interruptions to behavioral advantages (cf. lines 399-424). We therefore set out to investigate the underlying white matter, how it differed between children with and without interruptions, and its associations with reading skills.

Since long-distance projection connections tend to terminate more in gyri than sulci, one potential hypothesis was that gyral gaps in pOTS could be a hot-spot for such connections, facilitating the information flow between regions of the OTS and other functional hubs of the reading network. Because a higher density of such projection fiber endings is expected to result increased intra-cortical myelination, we test whether MD values in the gaps vs. sulcus are consistent with a higher myelination in the gaps than in sulcus, but we instead find the opposite pattern of lower myelination (cf. lines 435-457). This invalidated our first hypothesis.

In this context, it is thus unclear which questions would warrant additional analyses on MD values in other anatomical regions, or what these would bring in our specific search for mechanisms underlying the reading advantage of pOTS interruptions.

A second potential mechanism was that left pOTS gaps could be associated with increased local connectivity surrounding the left pOTS, through the packing of more U-shaped fibers traveling superficially, resulting somehow in a computational advantage for reading. This time, we found evidence in favor of this hypothesis: children with an interrupted left pOTS had more local white-matter connectivity around the pOTS travelling superficially under the left pOTS and it gaps (cf. lines 477-493). Moreover, when accounting in the same model for T3 reading on top of the presence of interruptions, this increase in local U-shape fibers was instead captured by T3 reading scores rather than the presence of a pOTS interruption. As such, these white matter differences did indeed explain differences in T3 reading, suggesting a candidate local-connectivity pathway underlying the reading advantage.

Comment (9) Were any of the analyses performed on the right pOTS? What are the differences in the laterality of gaps? Connectivity?

The right pOTS had an interruption rate of 58.3%, which was similar to that of the left pOTS (56.5%, Fisher test: p = .75, cf. Supplementary Figure 1 and lines 134-139).

The right pOTS does not show associations with reading skills, which we report in Figure 2C and lines 184-186:

“[A]ssociations between sulcal interruption and reading skills were specific to the left pOTS within VTC. No significant associations were observed for anterior OTS (aOTS) or MFS in either hemispheres, or for the right pOTS (see Figure 2c, all p-values > 0.58, all ΔR² < 0.7%).”

Due to the absence of an association between the right pOTS and reading abilities, additional connectivity analyses in the right hemisphere did not seem warranted.

Comment (10) Finally, the authors' conclusion, and particularly the last section of their discussion on the neuronal recycling hypothesis, does not seem related to their data, analyses, or questions. The authors do not motivate the link between a hypothesis focused on changes in functional activation during skill acquisition, to their current work which only has structural and diffusion connectivity data. Either remove or further motivate this discussion.

While there has been a heated debate on the specific nature and underlying mechanisms of “neuronal recycling”, our intention was merely to frame our results within the general well-established and widely accepted premises that (i) cultural skills such as reading and symbolic number processing are too evolutionarily recent to rely on dedicated neural circuits and therefore must recruit pre-existing cortical territories, and (ii) reading acquisition is accompanied by the development of functional responses to written words in left posterior vOT, around the pOTS, free from dedicated evolutionary constraints.

Keeping in mind that the left pOTS and surrounding cortex see a major functional development of functional responses to words literacy acquisition is indeed fundamental in order to understand the relevance and implications of our structural results in this particular patch of cortex that hosts the VWFA, and their relative cognitive specificity to reading. Specifically, we claim that strong structure-function associations around the left pOTS for reading may mediate the behavioral benefits of left pOTS gyral gaps.

We therefore refer to these questions and hypotheses throughout our text. We first mention the existence and importance of structure-function relationships in the case of the VWFA early on in our introduction (lines 57-66). Throughout the paper, we state our hypotheses on how sulcal morphology and the associated structure of white-matter fiber tracts may result in functional and behavioral reading benefits, motivating our white-matter connectivity analyses. The discussion paragraph “Local connectivity differences at gyral gaps: a computational advantage?” (lines 629-648) then explicits in depth our final interpretation linking our sulcal marker and the computational efficiency of the functional reading network, as supported by an extensive literature.

To avoid any implication that our findings speak directly to the neuronal recycling framework, we have revised the relevant sentence (lines 651-659) and conclusion to focus solely on its broad, non-specific premises and have removed explicit mention of neuronal recycling.

“Interestingly, associations between sulcal interruptions and behavior have also been reported for symbolic, but not non-symbolic, number processing (Roell et al., 2021; Schwizer Ashkenazi et al., 2024), highlighting common processes by which cultural acquisitions, too recent on the scale of human evolution to rely on dedicated neural circuits (Dehaene & Cohen, 2007), may be boosted by the presence pre-existing gyral gaps. In the case of the left pOTS, various other aspects of early brain structure have been proposed to constrain the development of reading skills and of functional activations for reading in the VWFA and broader neural network involved in reading such as anatomical connectivity (Bouhali et al., 2014; Grotheer et al., 2021; Li et al., 2020; Moulton et al., 2019; Saygin et al., 2016) and cortical morphology. In terms of the latter, longitudinal studies following pre-reading children at familial risk of dyslexia showed for instance that the surface area of the left fusiform gyrus (Beelen et al., 2019) and patterns of grey-matter volume around the VWFA (Skeide et al., 2016) could be predictive of future dyslexia diagnosis.”

We have also updated the subsection header to “Common cortical constraints on cultural learning” to reflect this more neutral framing, and adjusted the first discussion paragraph and the conclusion to avoid confusion with the neuronal recycling hypothesis. These changes clarify that our discussion situates the findings within a general conceptual background, rather than interpreting them as evidence for a specific theoretical model.

Comment (11) I think this paper could add interesting knowledge for the specific subfield of reading and the brain. However, the current state of the results, especially with the inclusion of so many trending results and the comparison of so many different processing pipelines and models, in addition to a conclusion that is not motivated by the work makes it difficult to appreciate the paper.

We thank Reviewer 1 for their suggestions to improve the manuscript. We have revised the text to focus more clearly on the main longitudinal and anatomically specific findings, and have clarified the role of the initial minimal-reader subgroup, the significant longitudinal contribution of pOTS interruption beyond associations with emerging literacy at age 5, and its unique contribution relative to other established predictors of reading. We hope these changes make the central contributions of the study clearer.

Although the revision adds some content to an already detailed article, we believe that, taken together, these analyses provide a thorough and integrated account of the association between OTS morphology and reading. In particular, they help clarify how macro-anatomical differences in sulcal morphology may relate to cognition, how these associations unfold across development, and how a candidate white matter pathway may contribute to this relationship.

Minor points:

Comment (12) Figure 1 needs more explanation for those who have not hand-labeled these regions. Can you clarify what differentiates the continuous left pOTS in the top row and then interrupted pOTS in the bottom row? The top row all has a gap between dark green and light green. Also, what does the color scale mean? Is it a posterior to anterior gradient?

We thank Reviewer 1 for highlighting the need for clarification. Our legend now stipulates:

“Left hemispheric views from exemplar children are shown, either with a continuous left posterior OTS on the top row (i.e., no more than one connex OTS component in the space posterior to the white dotted line) or an interrupted left pOTS on the bottom row (two or more sulcal components present in posterior space, with a total Euclidean distance between components ≥1mm). Green and orange gradient colors are respectively used to highlight the different sulcal components of the OTS and MFS.”

Comment (13) The discussion on sulcal interruption associations with symbolic but not non-symbolic number processing is interesting! Are these sulcal interruptions present in non-human primates?

To our knowledge, pOTS interruptions directly analogous to the human left pOTS gyral gaps studied here have not been systematically characterized in non-human primates. Macaques do have an occipitotemporal sulcus, and comparative work shows that sulcal landmarks in macaque and human VTC can relate to functional organization. However, the human OTS is laterally displaced relative to the macaque OTS, and the specific left pOTS interruptions examined here are defined in relation to human VTC and literacy. We therefore view the comparative anatomy of these interruptions as an open question.

Comment (14) Your T1 voxel size (line 629 0.859 x 0.859 x 1.2mm) does not match the recommendation for the FreeSurfer pipeline you stated, being both anisotropic and having a dimension with > 1mm. "The method works well for voxel sizes 0.75 mm3. It should work with voxel between 1mm3 and 0.75mm3 ... We haven't tested the stream for inputs with anisotropic voxels." (https://surfer.nmr.mgh.harvard.edu/fswiki/SubmillimeterRecon). Further, you note in the methods section that small interruptions can be a result of bad segmentation (line 718/719). Given that segmentation is affected by voxel size, and potential partial volume effects. How do the voxel parameters impact the results and reliability of the analyses?

Our T1 voxel volume was 0.885 mm³, within the voxel volume range for which the FreeSurfer submillimeter stream is expected to work, although we acknowledge the caveat that the stream was not specifically validated for anisotropic voxels. Yet, Freesurfer pipelines resample anisotropic voxels to isotropic ones by default, resulting here in a final voxel size of 0.859mm isotropic on which the submillimeter pipeline was run. To address possible segmentation concerns, we visually inspected all segmentations in bilateral ventral occipitotemporal cortex thoroughly, excluded scans with excessive motion, imposed a conservative> 1 mm criterion for classifying interruptions, and verified high T1–T3 reliability. Thus, while voxel anisotropy may affect very fine morphometric estimates, our macroanatomical feature of interest - the binary pOTS interruption classification - appears robust.

Comment (15) On line 417, you should refer to the panel of the figure (I think 4c bottom panel), like you did for many other results. It was helpful when you linked a particular result to its matching figure.

We thank Reviewer 1 for pointing out this omission, which has now been corrected.

Comment (16) The percentage values on the bars should be larger for Figure 2, they are hard to read.

We had chosen to represent the p-value significance on the bars, rather than the percentages themselves, which are indicated by the x-axis and reported numerically in the main text (except from the least relevant ones). We have now increased the font size of these significance stars. Thank you.

Reviewer #2 (Recommendations for the authors):

The authors may want to consider the points below.

Comment (1) The relationship with Performance IQ is interesting. It does not predict much variance in reading scores at T3 but it is strongly predicted by the pOTS interruption at T3. There is quite a significant correlation among all the measures. The authors acknowledge the difficulty in assessing the unique contribution of each measure. I was unclear how they "over" controlled for pre-literacy skills etc. (line 296) and would like more elaboration on that in the main text.

It would be interesting to know whether there were any cognitive measures where better performance was not predicted by the presence of the interruption? Were there any measures where worse performance was predicted? (i.e. a potential cost of this feature).

A relative specificity of left pOTS interruption on reading:

We agree that the association between left pOTS interruption and performance IQ at T1 raised the question of the cognitive specificity of a reading advantage associated with left pOTS interruption, as opposed to a possibly more general cognitive advantage as suggested by Reviewer #2 in their public review above.

This question is of course complicated by the fact that reading skills are by nature highly correlated with general cognitive abilities, as they are also with math abilities (see e.g., the meta-analyses by Ünal et al., 2023) and language. General cognitive skills and reading are in fact so intertwined that they positively and symbiotically influence each other over development (Ferrer et al., 2007; Peng and Kievit, 2020). Yet, bearing these strong associations in mind, our results suggested a certain degree of cognitive specificity of left pOTS interruption benefits on reading. Indeed, while left pOTS interruption predicted about 14.3% of variance in T1 concept formation (measuring performance IQ), it predicts about 20.5% of T3 TOWRE reading scores. In addition, left pOTS interruption significantly and strongly predicts T3 reading scores, while T1 performance IQ did not (cf. Figure 3A, D and C, except in the subsample of initial minimal readers where pIQ has a significant contribution but about twice smaller than that of pOTS interruption - Figure 3F). Therefore, the prospective association between left pOTS interruption and reading skills could not merely be driven by an association with general cognitive abilities at age 5. Finally, left pOTS interruption showed no other significant association with the pre-literacy skills considered (other than early literacy itself), or family history of dyslexia. This points towards a strong and relatively specific contribution of left pOTS on reading acquisition beyond its moderate association with T1 general cognitive skills.

We also conducted a new analysis to directly address this question, by systematically testing the associations between left pOTS interruption and all the cognitive and linguistic scores that were obtained at T3. Our new results also support the conclusion of a relatively specific cognitive advantage on reading, and are shown in Supplementary Figure 6 (with Supplementary Table 2 providing a description of the different subtests). The results are exposed in the main text as follows, in a new result subsection “Left pOTS interruption has a relatively specific cognitive impact on reading abilities” (lines 369-397):

“The incidental observation of a significant association between left pOTS interruption and performance IQ at T1, although smaller in magnitude and not sufficient to account for the association with literacy skills, raises the possibility that left pOTS interruption may confer a broader cognitive advantage rather than a specific benefit for reading acquisition. We therefore conducted a supplementary analysis to examine the relative domain-generality versus cognitive specificity of this association. This question is inherently difficult to address because reading and general cognitive skills are strongly correlated and mutually influence each other across development (Ferrer et al., 2007; Peng & Kievit, 2020; Ünal et al., 2023).

“We gathered all cognitive and linguistic scores obtained at T3, including measures of mathematics, general cognition, executive functioning, language, and reading (see Table S2 for a full list and description of the included subtests), and tested how each measure was associated with left pOTS interruption, residualized for demographic variables and total brain volume. Left pOTS interruption showed strong and significant associations with several measures of language, reading, mathematics, and general cognitive ability (see Supplementary Figure 6). As expected, we also observed strong and significant correlations among the behavioral measures themselves.

“However, the strongest correlations with left pOTS interruption residuals were observed for reading scores. Moreover, hierarchical clustering grouped left pOTS interruption with a subcluster that included most reading assessments - spanning phonological decoding, word reading, and sentence reading fluency -, as well as spelling and more surprisingly an expressive language index. This reading-related cluster was most closely related to another cluster comprising measures of written and oral language comprehension (i.e., receptive language), followed by a cluster of phonological awareness. In contrast, measures of mathematics, general cognitive ability, backward working memory and rapid naming formed a separate cluster. Thus, although left pOTS interruption is associated with several cognitive, linguistic, and academic measures, its pattern of associations is most closely aligned with children’s reading outcomes, supporting a relatively specific cognitive advantage for reading.”

We have therefore modified the Discussion paragraph that refers to the question of cognitive specificity vs. domain-generality as follows (lines 564-580):

“Interestingly, left pOTS interruption also showed associations with other cognitive skills: it was associated with performance IQ at age 5 (see Figure 3B and E), and with performance IQ, math and language skills more broadly at age 8 (Supplementary Figure 6). However, left pOTS interruption was most strongly associated and clustered with assessments of reading at age 8 (as well as spelling and expressive language). In addition, the prospective association between left pOTS interruption and reading skills was not merely driven by an association with general cognitive abilities at age 5 (Figure 3C and F) and no association with any other pre-literacy skill was found (Figure 3B and E). Math, reading, language and cognitive skills are intrinsically highly intercorrelated, as we also observed at age 8, and are known to mutually and positively influence each other over time (Ünal et al., 2023; Peng & Kievit, 2020; Ferrer et al., 2007; Huettig & Hulstijn, 2025; Dehaene et al., 2015). The weaker pOTS cognitive associations may therefore result from the mere combination of a specific pOTS influence reading and of associations between reading and other cognitive domains, although more research is needed to better understand these associations and how they unfold during development. Together, these findings highlight a relative degree of specificity of left pOTS influences to reading abilities, in line with the welldocumented functional specificity of the left pOTS for orthographic processing and reading (e.g., Dehaene & Cohen, 2011; Gaillard et al., 2006; Pillet et al., 2024; Wilson et al., 2013; Woolnough & Tandon, 2024; Zemmoura et al., 2015; Zhan et al., 2023).”

No observed cognitive cost to left pOTS interruption:

These different analyses show that there is no negative cost to the presence of left pOTS interruption, or at least not across the wide variety of cognitive skills we considered. While left pOTS interruption was significantly and positively associated with many assessments of general cognition, math and language (perhaps due to inherent associations and interactions between these domains), several domains were not significantly associated with the morphology of the left pOTS: rapid naming, backward working memory, as well as receptive vocabulary and phonological awareness (at least at T1). Except for a nonsignificant correlation of -0.01 with CTOPP Blending Words at T3, no subtest showed negative associations with left pOTS interruption.

“Over-controlling” and assessing unique contributions:

We had used the term “over-controlling” to refer to the fact that testing the longitudinal effects of left pOTS interruption on T3 reading over and above a number of strongly collinear covariates (such as letter knowledge, T1 reading scores and performance IQ) by nested model comparison necessarily decreased the estimation of the true effect of left pOTS interruption on reading. Indeed, the baseline model with collinear variables then already accounts for a part of the variability in pOTS morphology and of its effect reading, through its joint effects with other co-variates, even before the sulcal variable is explicitly added in the model. The statistical power to test the true sulcal longitudinal effect by nested model comparison over such a strong baseline is therefore decreased, and the effect is underestimated.

Since this non-canonical term and our previous explanations appeared confusing, we clarified the corresponding paragraph as follows (lines 336-361):

“These significant associations between left pOTS interruption, performance IQ and pre-literacy skills (Figure 3B and D), as well as potential associations between pre-literacy skills themselves (cf. correlation matrices in Supplementary Figure 5D and H), make it challenging to fairly assess the separate unique contributions of each of these variables to the longitudinal prediction of reading skills. For instance, because left pOTS interruption explains a significant amount of variance at T1 in letter knowledge, early TOWRE scores and performance IQ, some of its true direct effect on future T3 reading skills is already captured in a baseline model including these cognitive predictors only, even before left pOTS interruption is explicitly entered as a predictor. Yet, even when controlling in a such a stringent way for all pre-literacy skills, early reading abilities, family history of dyslexia and their shared variance with left pOTS interruption in such nested model comparison, left pOTS interruption still had a marginal additional contribution to predicting T3 TOWRE reading scores (ΔR² = 5.0%, F(1, 31) = 3.74, p = .062) in spite of this important collinearity. Rapid naming and family history were the only two other predictors that outperformed left pOTS interruption in terms of unique contributions to T3 reading (ΔR² = 7.7% and 6.6% for RAN and mother ARHQ respectively, see Figure 3C), possibly because these predictors were among the least confounded with others (see Figure S5D for correlations among predictors) and thus among the least affected by collinearity. Letter knowledge, in contrast, had the smallest, non-significant unique contributions to T3 reading (ΔR² = 0.61%, p = .50). In order to reduce the collinearity confounds resulting from the associations between pOTS interruption and T1 early reading skills, we also reran the same analysis in the subsample of initial minimal readers. Left pOTS interruption in this subsample significantly contributed to predicting future T3 reading over and above all pre-literacy skills and family history (ΔR² = 27.8%, F(1, 12) = 13.80, p = .003), making it the first independent longitudinal contributor of reading (see Figure 3F). The second largest longitudinal predictor in terms of unique contributions was performance IQ (ΔR² = 12.8%, F(1, 12) = 6.34, p = .027). No other predictor had a significant unique contribution to the longitudinal prediction of T3 reading in the subset initial minimal readers, including rapid naming even though its separate contribution was larger than that of pOTS.”

We also moved several figure panels from Supplementary Figure 5 to Figure 3 so that readers would have the necessary material in the main text to document this collinearity and see how it impacted the separate vs. unique contributions of each predictor to T3 reading.

Comment (2) It was surprising that no other anatomical feature of the pOTS (like sulcal depth) predicted reading skills. I would have expected these to be quite closely correlated with interruption distance that did predict reading. Do the authors have any thoughts as to why this might be?

We thank Reviewer 2 for this question. While it seems intuitive that gyral gaps would affect sulcal depth, this mostly depends on whether we consider these gaps to be part of the sulcus -which here we do not- and on how the depth measure is actually calculated. With a definition of the sulcus as exclusive of gyral gaps, sulcal interruptions affect sulcal depth profiles only locally around the interruptions, where the fundus has to emerge to the convex hull surface. Because we measure sulcal depth based on the depth of the 8% deepest vertices (using an approach adjusted from that of Madan, 2019, see Methods lines 845-852), our measure of sulcal depth is essentially unaffected by interruptions.

As a confirmation and for more details, we provide Author response image 1 for the correlation matrix between the various morphological measures under consideration. (Using the same conventions as other correlation matrices displayed in the article and supplements: only significant correlations are displayed, according to FDR-corrected p-values above the diagonal.)

Author response image 1.

Comment (3) I hadn't quite appreciated on first reading the quite large variability in the location of the interruption (see Figure 4a, where three clusters seem to emerge). Nor did I appreciate that more than one interruption was often present (perhaps Figure 1 could be updated to show examples with more than one interruption). Some measures of distance along the OTS could be helpful and a possible comparison of the "types" based on location. I would have thought that proximity to the location of the VWFA might have meant a stronger effect. I presume this could be tested or discussed.

We entirely agree with Reviewer 2 that these are important questions. Unfortunately, it also appears that these cannot be reliably tested in our sample.

Specifically, while 25 children out of 43 had at least one interruption in the left pOTS, only 3 of those had two or more interruptions larger than 1mm each (or 6 children with two interruptions of any size). These incidence rates, combined with the fact that the locations of pOTS gaps do not distribute uniformly along the postero-anterior axis (Figure 4A), do not allow us to reliably assess in this sample either whether having more interruptions may confer an additional reading behavioral advantage, or whether interruptions in particular locations of the pOTS could be more beneficial than others.

We explored - for speculative purposes - whether a relationship may exist between reading scores and the location of left pOTS interruptions, taking the center of mass of the cortical gyral gap volumes as a coarse reference. We found no evidence for any relationship between reading and the locations of the left pOTS gap along the antero-posterior axis, nor between reading and the distance of the gap centroids to the VWFA (taking the Neurosynth reading meta-analysis peak coordinates, MNI -44 -58 -12), or between reading and the distance to the VWFA standard coordinates along the Y axis only (please see Author response image 2).

We choose not to report these analyses in the main text as they seem largely underpowered.

However, we added an example participant with two left pOTS interruptions in Figure 1 as suggested, and now added reference to these important questions in the Discussion, for future studies to address (lines 596-600):

“Such large-N approaches are needed to answer a number of outstanding questions, such as, in our case, whether there is an additional behavioral reading benefit to having two or more left pOTS interruptions - since these were too infrequent in our sample -, or whether gyral gaps placed in specific locations along the left pOTS may be optimal to for facilitating reading acquisition.”

Author response image 2.

Comment (4) It wasn't clear to me how the analysis of the diffusion data proceeded in the case of more than one interruption - it appears that each one was measured but this could be clarified. Is the location of relevance to the findings?

Regarding diffusion analyses, the diffusion tensor analysis averaged values across all pOTS interruptions together in the few children who had several. The tractography analysis used the full pOTS and all its interruptions, if present, together as a seed volume.

The precise location of the gyral gaps would indeed be very relevant to the tractography findings as one expects the gyral gaps to relate in a local fashion to the neuroanatomy of the underlying white matter. However, using the whole pOTS with its gaps as a seed seemed to us the only reasonable way to investigate the white-matter correlates of the effect of gyral gaps on reading at a group level, given (i) the large variability in gap location among the 15 of children with interruptions and diffusion data, (ii) the fact some children had multiple gaps, and most crucially (iii) the need to find a common ground for comparison with the group with no left pOTS interruption (continuous sulcus). The fact that our analyses average along the whole pOTS and across children with different pOTS gap locations likely washes away some of this neuroanatomical specificity, thus reducing the strength of any expected effect.

Comment (5) The authors could include a discussion of the sample's characteristics. They are not necessarily representative given the high SES and the average PIQ being more than 1SD above the mean.

We thank Reviewer 2 for pointing out this limitation we had overseen.

High-SES and high-functioning population samples indeed constitute a common bias in pediatric research samples, since study participation requires parents to have the time, interest and access to necessary information. This bias was likely increased here by the fact the data was acquired at Stanford University, in a very privileged area (Palo Alto, CA). The median performance IQ was indeed about one standard deviation above the population mean. Moreover, our sample is enriched for family history of dyslexia. We agree with the reviewer that this limits the generalizability of our results.

Yet, we replicate the association between left pOTS interruption and reading skills observed by Cachia and colleagues (2018) in a sample where half of the participants were from a rural and (very) low socioeconomic background (so that they would match a sample of illiterate adults), and with limited higher education. This suggests that, overall, such associations may generalize across extremely varied socioeconomic backgrounds and also possibly along the spectrum of general cognitive skills.

Since our reviewed preprint came out, two other studies further replicated associations between the left pOTS and reading skills (Cachia et al., 2025; Yao et al., 2026), in populations of different ages, countries and across the reading spectrum, including many children with dyslexia (Yao et al., 2026). While SES and cognitive skills are not systematically reported in those studies, one could assume that these studies and ours pooled together would be more representative.

Accordingly, we added this paragraph to the discussion (lines 548-562):

“Our study further extends previous results by Borst, Cachia and colleagues (2016; 2018) to a population of children with above-average cognitive and reading scores, from relatively high-SES families, and enriched for family history of dyslexia (cf. Table 1) - although no child met criteria for dyslexia by T3. While our sample is not representative of the general population, thereby limiting the direct generalizability of our results, half of the adult sample from Cachia et al. (2018) came from low socio-economic and rural backgrounds (matched to a sample of illiterate adults), suggesting that the association between left pOTS interruption and reading skills is robust across socio-economic contexts. Since our reviewed preprint came out, the association between left pOTS interruption and reading was further replicated (Cachia et al., 2025; Yao et al., 2026), notably in a larger child sample along the full reading continuum and oversampling children with dyslexia (Yao et al., 2026). (Of note, the finding that pOTS morphology correlated in adults with reading fluency rather than accuracy (Cachia et al., 2025) may also explain one of two prior negative findings concerning the association between pOTS and reading (Del Mauro et al., 2022)). Thus, our results together with the extant literature overall underline a common effect of left pOTS interruption observed across the continuum of reading abilities, and possibly of cognitive abilities.”

Minor

Comment (6) Line 342-44: A visualisation of what is meant by superficial vs deep plis de passage would help.

While an illustration of deep vs. superficial plis de passage would greatly help in clarifying this distinction for the readers, we feel that providing such a visualization in our figures would be equally confusing, if not more, as it may prime readers to wrongfully assume that we differentiate between superficial and deep plis de passage in our own analyses. Instead, we have tried to further clarify the distinction between deep and superficial plis de passage in the text as follows (lines 418-424):

“Indeed, Bodin and colleagues (2021) showed that, in the superior temporal sulcus (STS), the presence of plis de passage was associated with a higher density of U-shaped fibers connecting adjacent gyri. Superficial plis de passage, i.e., complete sulcal interruptions with a gyral gap visible on the cortical surface, showed an even higher local connectivity advantage than deep plis de passage, the complete gyral gaps or partial interruptions with sulcal pinching which are buried within the depth of the sulcus. (Please note that in our study, we focus on superficial gyral gaps visible on the cortical surface only, and do not classify deep plis de passage.)”

Comment (7) Line 96 - replace "blindly from" with "without awareness of" or "while .... were concealed".

The text was edited accordingly (lines 102-103 and 781) - thank you.

“[...] the OTS and MFS were delineated manually in each hemisphere, without awareness of the reading scores [...] Sulcal labeling was conducted without awareness of the children’s reading scores [...]”

(8) Line 547 - it is my impression that the findings of morphological differences in dyslexia are quite mixed. This gives the impression that the studies reported are representative of quite a vast number of studies and I don't think that is the case. Perhaps a sentence here with some more scepticism or alluding to the diverse findings in dyslexia?

It was indeed not our intention here to simplify or summarize a broad literature on morphological differences in dyslexia, but rather to cite a few example results in support of the preceding assertion “various other aspects of early brain structure have been proposed to constrain the development of reading skills”.

We clarified this sentence as follows (lines 659-662):

“[L]ongitudinal studies following pre-reading children at familial risk of dyslexia showed for instance that the surface area of the left fusiform gyrus (Beelen et al., 2019) and patterns of grey matter volume around the VWFA (Skeide et al., 2016) could be predictive of future dyslexia diagnosis.”

Comment (9) Finally, there is quite a lot of supplemental information, some of which is very interesting. I would recommend that the authors check what could be usefully transferred to the main body of the article. eLife uses figures and figure supplements followed by Appendices and the authors might want to check this before deciding on the final version of record.

We thank Reviewer 2 again for this suggestion to improve our manuscript. We have chosen to move several figure panels for Supplementary Figure 5 to Figure 3, following this suggestion, and given that our previous explanations in the paragraph concerning reading predictors appeared confusing to both reviewers (cf. see Rev 2 recommendation comment (1) and rev 1 recommendation comment (4)).

While figure supplements seem handy for reading the article directly on the eLife website, we chose to stick with the more standard practice of one appendix or supplementary file gathering all the additional information, which seems more accommodating of different reading practices overall.

References for Response to Reviews:

Borst G, Cachia A, Tissier C, Ahr E, Simon G, Houdé O (2016) Early Cerebral Constraints on Reading Skills in School-Age Children: An MRI Study. Mind, Brain, and Education 10:47–54.

Cachia A, Dupont C, Palmis S, Menu I, Auzias G, Sein J, Coulon O, Longcamp M (2025) The sulcal patterns of the occipito-temporal and anterior cingulate cortices influence reading and writing in children and adults. Cereb Cortex 35:bhaf145.

Cachia A, Roell M, Mangin J-F, Sun ZY, Jobert A, Braga L, Houde O, Dehaene S, Borst G (2018) How interindividual differences in brain anatomy shape reading accuracy. Brain Structure and Function 223:701–712.

Del Mauro G, Del Maschio N, Abutalebi J (2022) The relationship between reading abilities and the left occipitotemporal sulcus: A dual perspective study. Brain and Language 235:105189.

Ferrer E, McArdle JJ, Shaywitz BA, Holahan JM, Marchione K, Shaywitz SE (2007) Longitudinal Models of Developmental Dynamics Between Reading and Cognition From Childhood to Adolescence. Developmental Psychology 43:1460–1473.

Peng P, Kievit RA (2020) The Development of Academic Achievement and Cognitive Abilities: A Bidirectional Perspective. Child Development Perspectives 14:15–20.

Reuter M, Schmansky NJ, Rosas HD, Fischl B (2012) Within-subject template estimation for unbiased longitudinal image analysis. NeuroImage 61:1402–1418.

Roell M, Bellon E, Polspoel B, Declercq M, De Smedt B (2022) Investigating the association between variability in sulcal pattern and academic achievement. Sci Rep 12:12323.

Ünal ZE, Greene NR, Lin X, Geary DC (2023) What Is the Source of the Correlation Between Reading and Mathematics Achievement? Two Meta-analytic Studies. Educ Psychol Rev 35:4.

Yao JK, Mitchell JL, Davison A, Yeatman JD (2026) Sulcal anatomy of ventral temporal cortex and reading development. :2026.04.06.716640 Available at: https://www.biorxiv.org/content/10.64898/2026.04.06.716640v1.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, T. Wijerathne et al. investigated and reported the agonistic effect of Yoda1 and Yoda2 over PIEZO2 function using patch clamp electrophysiology, Ca2+ imaging, and molecular dynamics. They find that Yoda1 sensitizes PIEZO2 to membrane tension, can induce Ca2+ influx, and decreases its inactivation to a lesser degree than it does to PIEZO1 channels. Additionally, their data shows that Yoda2 sensitizes PIEZO2 channels to membrane indentation to a greater extent, but it has a weaker effect on channel inactivation than Yoda1. Interestingly, they report that a mutation in a conserved arginine between PIEZO channels can be used to abolish PIEZO1mediated Ca2+ flux in response to Yoda molecules. As a whole, the results presented here should be put into perspective against previous and future works involving systems where both PIEZO1 and PIEZO2 might be expressed. This is especially true for works where Yoda1 has been used as a basis for determining the absence of PIEZO2.

Strengths:

The authors use multiple techniques to investigate how Yoda molecules affect the three most important biophysical aspects of PIEZO channels that, when changed, result in pathophysiological responses: a) sensitivity to mechanical stimuli, b) Ca2+ entry, and c) channel inactivation. Lastly, they find a specific amino acid/region that could be exploited for drug design and/or development.

Weaknesses:

The methods and discussion sections are lacking enough detail to fully evaluate the findings and put them into perspective, respectively.

We have included new results, expanded our discussion, and added additional details in our Methods section.

Reviewer #2 (Public review):

Summary:

This manuscript challenges the long-standing assumption that Yoda1 and Yoda2 are PIEZO1selective activators. Using patch-clamp electrophysiology and calcium imaging in HEK293TΔPZ1 cells overexpressing PIEZO2, the authors demonstrate that Yoda1 potentiates PIEZO2 stretch activated currents to a similar extent as PIEZO1 and slows PIEZO2 poking-current inactivation (albeit with lower efficacy). They further show that the more potent analog Yoda2 affects PIEZO2 at nanomolar concentrations and use mutagenesis and molecular dynamics simulations to propose that Yoda2's benzoic acid group forms a transient salt bridge with R1724 in the putative Yoda binding pocket, explaining its enhanced potency.

Strengths:

The authors are established Piezo/biophysics experts; the study is highly important, technically competent, and carries significant implications for the reinterpretation of prior work that used Yoda compounds as PIEZO1-selective probes.

The core finding that Yoda1 modulates PIEZO2 stretch currents is convincing and important. However, several conceptual, methodological, and presentational issues need to be addressed before acceptance, as detailed below.

Weaknesses:

(1) The abstract states that Yoda1 potentiates PIEZO2 "as efficaciously as PIEZO1." This claim is accurate only for stretch currents and single-channel open probability, but the paper itself demonstrates important asymmetries: i) Yoda molecules slow PIEZO2 poking-current inactivation ~2-fold, versus ~5-10 fold for PIEZO1 (Figure 3b and ref #60). ii) Spontaneous Ca²⁺ entry via PIEZO2 requires non-physiological conditions (high extracellular Ca²⁺, hypertonic solutions) that are unlikely to occur in native cells. The abstract should be revised to clearly qualify where equivalence holds and where efficacy differences exist. IMO, the current wording risks overcorrecting the historical bias (PIEZO1-only) by going too far in the other direction.

We have changed our language throughout the manuscript to convey more accurately differences of Yoda agonism between the two Piezo homologs.

(2) Related concern: the PIEZO2 Ca²⁺ signal in Figure 2 is only detectable using a Ca²⁺-boosted solution (CBS ie 30 mM Ca²⁺). Physiological extracellular Ca²⁺ and cells normally do not experience sustained hypertonicity at these magnitudes. The authors should explicitly clarify that the practical implication of their findings is primarily for electrophysiological (patch-clamp) experiments and that the Ca²⁺ imaging caveat applies only under amplified conditions. Specifically, the authors should state that in standard Ca²⁺ imaging assays with physiological buffers, PIEZO2 is unlikely to confound Yoda1 results.

Agreed. As mentioned above, we have modified our wording to convey this point more clearly.

Related point: Can cytochalasin D (CytoD) restore a Yoda1-dependent Ca²⁺ signal in physiological saline? This would help determine whether the weak PIEZO2 response is primarily a membrane tension issue (cytoskeletal tethering) versus intrinsically lower channel expression or permeability. The authors already have tagged PIEZO1/2 constructs and could, in principle, normalize by surface expression.

We have repeated our acute pharmacological treatment in cells pre-treated with CytoD (or 0.5% DMSO vehicle control). These experiments were done in normal saline solution. We found that Yoda1 produces a very small (but significant) calcium influx in cells treated with CytoD. This result strengthens our conclusion that Yoda1 is capable of producing an activatory effect on Piezo2 in absence of external mechanical stimulation - albeit this effect is very small and only detectable in non-physiological (calcium-rich or destabilized cytoskeleton) conditions. It remains difficult to definitely conclude about why Yoda molecules exert different agonistic effects. We can only discuss possibilities. Differences in Ca2+ permeability is unlikely to contribute to this difference, as pore properties and selectivity for monovalent ions are similar between the two channels (see PMID: 39543876). Slight differences in how Yoda bind the Yoda binding region could explain why Yoda1 robustly modulates Piezo2 stretch currents but fails to produce robust calcium influx, as recent work suggests that these two agonist effects may originate from two distinct Yoda binding poses in this region (PMID: 38060566; PMID: 41402296). Piezo2’s intrinsically high threshold for stretch-activation could also represent a contributing factor, as figures 1e-f show that Piezo2’s midpoint activation pressure in the presence of Yoda1 (about -30 mmHg vs. -60 mmHg) might still be too high to enable robust Yoda-induced activation at the resting membrane tension of the cell. Since Piezo1 has been consistently shown (by us and others) to be expressed at a higher level than Piezo2 in transfected HEK293 cells (e.g., PMID: 20813920; PMID: 32227462, PMID: 37102984; PMCID: PMC13423835), we have not replicated these experiments with Piezo1. We have modified our manuscript to include these new results and discussion.

(3) The mean inactivation tau values for wild-type PIEZO2 poking currents in both DMSO and Yoda1 conditions (Figure 3b, approximately 15-40 ms range) appear substantially higher than values reported in published literature (typically 5-10 ms; eg, PMID: 20813920). This discrepancy needs to be addressed.

This discrepancy likely arises because inactivation kinetics of Piezo1 and/or 2 poking currents can be modulated by many biological and experimental variables that are difficult to control. Biological variables include membrane potential (PMID: 20813920), extracellular pH (PMID: 25561736), temperature (PMID: 35858335; PMID: 31413193), the presence of modulatory proteins (PMID: 37590348) and extracellular matrix (PMID: 28164706). Experimental variables include the mechanics of probe displacement (velocity and impact angle) and the precise positioning of the time-cursor near the peak current for exponential fitting. In addition, the decaying portion of Piezo poking currents is likely contributed by both inactivation and deactivation, as a recent study demonstrates relaxation of the poke stimulus during mechanical indentation in N2a cell (PMID: 42649207). Cellular viscoelastic properties and cytoskeletal organization are thus anticipated to dictate how fast this relaxation occurs, influencing the proportion of inactivating and deactivating currents in poking recordings. Since this point deviates from our main goal - to test an effect of Yoda on channel kinetics measured side-by-side – we prefer not to discuss it.

(4) The authors perform all MD simulations on a truncated PIEZO1 model and justify this choice by noting that the Yoda binding region is highly conserved between homologs. This is a reasonable and defensible starting point given the availability of well-validated PIEZO1 simulation set ups in their lab. A few points are nonetheless worth addressing: While PIEZO2 simulations are not strictly required, the authors are encouraged to briefly discuss whether any long-range structural differences between PIEZO1 and PIEZO2 (outside the binding site itself) could influence Yoda2 binding dynamics, particularly in light of the chimera data showing that PIEZO2 sequence in repeat A abolishes Yoda1 sensitivity. This reviewer still doesn't understand the reason behind this discrepancy despite it being acknowledged in the text.

We have now conducted three replicas of all-atom MD simulations of the Yoda2-bound PIEZO2 system. The new results show that the equivalent Arg residue in PIEZO2 (R2029) also forms a salt bridge with Yoda2, consistent with our observations from the Yoda2-bound PIEZO1 simulations. Taken together, these simulation results seem to point to the fact that Yoda molecules bind to a similar region in both PIEZO1 and PIEZO2. The lack of Yoda1-sensitivity in the chimera is quite puzzling, and we can only speculate about why. The swapped chimeric region includes 103 residues, 21 of which are non-conserved between PIEZO1 and PIEZO2 and distributed around the binding region (PMID: 29795280). These mutations could collectively and allosterically alter the binding free energy landscape in a manner that either 1) strongly reduce Yoda binding affinity or 2) equalize Yoda binding affinity for both curved and flat conformations, effectively rendering Yoda molecules silent binders (similar to how we previously described Dooku1 binding to Piezo1 PMID: 38060566).

Another MD-related comment is that three simulation replicas (which is impressive for such a big system) show markedly different salt bridge occupancy (82.6%, 49.7%, 99.8%; stated in the text). This wide variation suggests incomplete sampling in at least one replica. The authors should provide RMSD plots for ligand and protein backbone to assess convergence and possibly discuss whether the 49.7% replica represents a genuinely distinct binding mode or incomplete equilibration.

We have extended PIEZO1-Yoda2 replica #2 from 600 to 1400 nanoseconds. This replica shows that the salt-bridge turned ON and OFF during the simulation because the Arg side chain tends to flip. This flipping behavior is evident in the 20 µs Replica #1 (Figure 6c). In Figure 6-figure supplement 1, we analyzed our previous five replicas of MD simulations using the PACE force field. We show that the angle distributions indeed vary between replicas and subunits at the timescales currently affordable by MD technique for this large system. Therefore, it is not too surprising that the salt bridge occupancy differs between three all-atom simulations. We now provide RMSD of ligand and protein backbone for each Replica as Figure 6 supplement 1. The time evolution of Yoda2 binding poses across all simulation replicas are now illustrated in Figure 6-figure supplement 2, which shows that Yoda2 is mobile, yet remain stable in this overall hydrophobic binding site, consistent with our previous report (PNAS2023 PMID: 38060566). We also added all corresponding analysis of Yoda2-PIEZO2 in the same figures.

(5) The Discussion proposes that PIEZO2's weaker Ca²⁺ response to Yoda1 could partly reflect lower membrane expression. Since the authors already have fluorescently tagged PIEZO1 and 2 constructs, a simple fluorescence intensity comparison between the two (acknowledging it would reflect total rather than surface expression) could provide at least indirect support for this claim. Alternatively, if such a comparison is not feasible, the authors may consider removing membrane expression from the list of proposed explanations or explicitly acknowledging that this remains unsubstantiated speculation. The max poking currents may somewhat and roughly indicate the level expression difference too, if done exactly side by side.

PIEZO2 expression is known to be lower than PIEZO1 in heterologous systems (PMID: 20813920; PMID: 32227462, PMID: 37102984; PMCID: PMC13423835), hence we have not attempted to test if this was the case with our tagged constructs.

(6) The abstract or concluding remarks should highlight that Dooku1 is not PIEZO1-selective in its agonist-like action on PIEZO2, and that Cmpd15/Cmpd64 appear to be better PIEZO1-selective tools. This nuance is buried in the Results section.

We now list these results in the abstract.

(7) The authors should not cite PMID 31015490. Clearly, any work on MCC13 is confounded by the overwhelming expression of PIEZO1 (PMID: 42084270). Instead, the authors should also cite the literature from others who have clearly recorded stretch currents from PIEZO2 before the cited studies (eg, PMID: 37590348).

Agreed!

Reviewer #3 (Public review):

Summary:

The manuscript reports that Yoda1 and Yoda2 agonize PIEZO2 in a manner similar to PIEZO1, increasing open probability and stretch sensitivity, but the mechanism underlying this sensitivity is incomplete. Mutagenesis was shown exclusively in PIEZO1, with no corresponding mutagenesis in PIEZO2, so the proposed mechanism in PIEZO2 is inferred by homology rather than directly tested. All experiments use mouse PIEZO2, and the human ortholog should be used before generalizing the proposed reinterpretation of the field.

Strengths:

The pressure-clamp electrophysiology demonstrating a shift in half-activation pressure for PIEZO2 is compelling evidence in support of the central claim.

Weaknesses:

(1) In the single-channel recordings (Figure 1a), it's unclear how many channels were present in those patches. After applying -60 mmHg pressure, multiple channels would be activated (as seen in Figure 1e). The number of channels in the patch and their inactivation rate could significantly influence the open probability in such experiments. To overcome this, in the original Yoda1 article (Syeda, Ruhma, et al. eLife 2015), no additional pressure was used.

To clarify the confusion, we record single-channel PIEZO2 currents less than 24 hrs after transfection and record macroscopic PIEZO2 currents 2-3 days after transfection. Hence, unlike the cited study, our single and macro currents are obtained from different patches. When patching cells for single recordings, most patches do not show any mechano-currents and those that do typically show only one current level of single-channel conductance through the recording, even when the patch is highly pressurized.

Additionally, the reported open probability comparison (n=7 Yoda1 vs n=17 DMSO patches) has an SEM nearly as large as the effect itself (0.30 {plus minus} 0.11), consistent with a small number of outliers driving this. The underlying mean open and shut times are reported without any statistical test; only the derived open probability receives a p-value. Additionally, in Figure 1a, the Yoda1 condition noise is different from the control. This should be stated if noise filtering was applied and how, given that this could affect open probability analysis.

This is a fair point. We have removed two outliers and have performed statistical analysis on mean dwell times. The effect of Yoda1 is still highly significant. We have replaced current traces with two of similar noise levels. We acquired all single-channel current traces at 100kHz, filtered them at 5kHz, and displayed them at 500 Hz.

(2) The calcium imaging data in Figure 2 raise significant concerns regarding the chemical activation claim. The calcium-boosted solution (30 mM Ca2+) is not physiological and appears to be generally stressing cells rather than specifically activating PIEZO2: the control condition under CBS already shows an elevated signal, consistent with cells being unwell at this calcium concentration, and adding Yoda1 on top of this shifted baseline raises further questions about specificity rather than confirming it. Separately, it is unclear why DMSO alone produces measurable PIEZO2-associated calcium influx in HBSS, a result that is not addressed in the text. Figure 2 should clearly indicate when DMSO/Yoda1 perfusion was initiated, and y-axis labels are missing from panels A and B.

We agree and have toned down our chemical activation claim, insisting that this activation is very weak in absence of external mechanical stimulus, being only detectable under extreme, non-physiological conditions. We also re-analysed our data (and added fluorescence scale bars, thank you) showing time-course and scatter plots from the same cells in Figure 2a. We think the “bump” seen upon DMSO perfusion in PIEZO2 cells could be amplified by the low expression of GC6 in these cells. We now discuss this point in our revisions.

(3) In the poke experiments, an activation threshold should be calculated and reported, and amplitude data (e.g., peak current versus indentation depth) should be shown rather than only inactivation tau values. It is also unclear why mClover3- and N-GFP-tagged constructs were used in these experiments, since electrophysiological recording already confirms channel expression without requiring a fluorescent tag.

Valid point, we are now comparing peak currents for different poking distances. We have removed our Tau analysis for our tagged-PIEZO2 clones.

(4) For inactivation kinetics (Figure 3b), the authors use unpaired comparisons across separate cells, whereas the deactivation experiments (Figure 3c) use paired; it should be applied to the inactivation experiments as well. Deactivation kinetics for PIEZO2 itself should be shown.

These experiments have different goals which do not require using the same protocol. Deactivation kinetics experiments were used for the chimera because this parameter was shown by us to be the most sensitive to Yoda1. Hence, if a Yoda modulation exists, but is hard to detect in the chimera, using this protocol with paired samples provide us with the highest detection sensitivity. This level of sensitivity was not needed to detect an effect of Yoda1 on PIEZO2.

If the claim is that Yoda1 acts on PIEZO2 through the same mechanism proposed for PIEZO1, then a PIEZO1/2 chimera should be expected to show a corresponding effect on deactivation tau; instead, this chimera is reported as completely Yoda1-insensitive despite both parental channels being Yoda1-sensitive, as shown in this study.

This discrepancy is acknowledged in the text. We do not know why the chimera is Yoda insensitive and can only speculate at this point. Of note, one must acknowledge that this chimeric swapping introduces 21 amino acid changes (vs. WT PIEZO1) which may have profound allosteric effect on binding affinity and/or efficacy. MD studies would be useful to explore this possibility in a future study.

(5) Given that this reflects a different experimental paradigm for Yoda EC50, PIEZO1 should be included within Figure 4b. Additionally, EC50 bar plots should be present on this figure.

Showing EC50 plots here is not possible because each cell was exposed to only one dose of Yoda1 (unpaired measurements). We have included a Yoda1 dose-response curve against PIEZO1 inactivation Tau from our prior study (PMID: 35858335) for comparison as a Figure Supplement.

The inactivation time constant for PIEZO2 without Yoda1 is inconsistent across figures, below 20 ms in Figure 3b but above 20 ms in Figure 4c.

As explained above in our answer to Reviewer #2, these inconsistencies likely occur because PIEZO inactivation kinetics are susceptible to modulation by a number of biological and experimental factors that are not easily traceable, making it difficult to define absolute channel kinetics.

(6) Finally, the modeling is performed exclusively on PIEZO1, whereas the manuscript's central focus is PIEZO2. It is therefore unclear whether the proposed structural mechanism, including the basis for Yoda2's reduced efficacy on PIEZO2, can be directly extrapolated to PIEZO2.

We have now conducted three replicate all-atom MD simulations of the Yoda2-bound PIEZO2 system. The new results show that the equivalent Arg residue in PIEZO2 (R2029) also forms a salt bridge with Yoda2, consistent with our observations from the Yoda2-bound PIEZO1 simulations. However, the current simulations do not allow us to distinguish differential efficacy of Yoda2 toward PIEZO1 versus PIEZO2. The reduced efficacy of Yoda2 on PIEZO2 may instead arise from differences in its binding affinity for the open versus closed conformations, or from contributions of cellular components that are not represented in our MD simulations, such as the cytoskeleton.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Main:

(1) Adding more depth and detail to the methods section will help others replicate the findings.

Agreed.

(2) Methods: line 325. Describe the way each compound was prepared for each concentration without undissolved particles. Avoid using the phrase "as described before" in the methods section.

Compounds were dissolved in DMSO and simply diluted in recording solution at the time of experiments with vortex mixing.

(3) Figure 1B (comparison of open probability): only three points out of 7 (with Yoda1) seem outside the data range of the control (DMSO). It seems very unreliable for an agonist. Moreover, in Figure 1F, the data seem very noisy. I would suggest adding more n.

We have eliminated two outliers and reanalyzed our data, showing statistics for mean dwell times and open probability.

(4) The authors should add to the "Yoda1 activates PIEZO2 in the absence of external mechanical stimulus" section (or the methods) how perfusion of Yoda1 was applied.

We used manual pipetting.

(5) Lines 165 - 171. This part should be moved to the discussion and expanded on. Particularly since the reference they allude to comes from the same group.

This discussion part is needed to introduce the chimera experiments and thus should remain in Results.

(6) Figure 3B. The noise range of the time constants of inactivation is a lot. Specially for transfected cells. I would suggest a couple of sentences explaining why the authors think this happens.

This discussion is now included.

(7) Figure 4C. Tau inac of DMSO control seems very high when compared to others. I would suggest a couple of sentences explaining why the authors think this happens.

One difference is that DMSO concentration here is higher (0.25% vs 0.075%) to match the higher concentration of Yoda1 tested. Inactivation kinetics are subject to modulation by many parameters; hence we focus on side-by-side comparisons instead of absolute values.

(8) Line 213. Which standard binding equation? Include in the methods.

Done.

Rethink calculating the EC50 with dose responses that saturate. Figure5C. Are these absolute or relative EC50s?

EC50 of mutants are normalized to WT.

(9) Discussion: "Our discovery that Yoda1 modulates PIEZO2 stretch currents as effectively as PIEZO1's strongly suggests that some of the reported biological roles attributed to PIEZO1 using this agonist could be (at least partly) transduced by PIEZO2. For instance, our discovery seamlessly reconciles the puzzling fact that reducing PIEZO2 expression in cells that co-express PIEZO1 also reduces the effects of Yoda1 (49, 76, 77). Along." In the referenced works (49, 76, and 77) its not checked if PIEZO1 levels remain the same when PIEZO2 was knocked out. Here, the authors should discuss this possibility.

Good point!

Minor:

(1) Indicate in the figure legends, result or methods section, what the error bars represent.

Done.

(2) Indicate the p-value for Figure 1B.

Done.

(3) Figure 2. Include the ionomycin value that each group is normalized against.

We provide now vertical scale bars for all samples.

(4) Why not use PIEZO2 for the MD simulations?

Done.

Reviewer #2 (Recommendations for the authors):

Minor comments

(1) In the Abstract: The sentence "Although a structural framework for PIEZO1 activation by Yoda1 exists" may be confusing for readers outside the field. The authors may mean "mechanistic" or "computational" framework. Please clarify or reword.

We have reworded the abstract.

(2) Residue number in abstract: The abstract states "a conserved arginine in the Yoda binding site" without identifying it. Please add the residue number (R1724 in mouse PIEZO1) for clarity.

Done

(3) Figure 1 legend or in the method: recording mode and filter settings: The figure legend should explicitly state that single-channel recordings were obtained in cell-attached mode, and should report the filter frequency (kHz) and sampling rate used for idealization. This is essential for readers to evaluate dwell-time analysis.

Done, but details are in the method.

(4) Several instances throughout the text use "native" where "naïve" is clearly intended.

Corrected, thank you.

(5) The statement that PIEZO2 requires more mechanical force than PIEZO1 (~−60 vs ~−40 mmHg P1/2) should be interpreted cautiously without this information, and the authors should clarify whether pipette geometry was controlled between PIEZO1 and PIEZO2 experiments.

We have shown that PIEZO2 requires more force to be opened by membrane tension relative to PIEZO1 using MscL gating as a tension-calibration system (PMID: 41703062). Pipette geometry is consistent for each type of experiment (macroscopic or single-channel recordings). We have expanded our Methods.

(6) The finding that Dooku1slows PIEZO2 inactivation similarly to Yoda1 is striking and is currently underplayed. This raises important questions: Does Dooku1 elicit Ca²⁺ entry in PIEZO2-expressing cells? It could at least be discussed further in the text.

Likely not, since Yoda-induced calcium influx is very weak and requires non-physiological conditions to be detectable. But this is worth trying at some point.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) Where the manuscript still has potential for improvement is the discussion, which in its current form does seem slightly self-contained and does not fully integrate the findings of previous studies on Drosophila rhodopsin7. As the introduction specifically points out that previous findings have been contradictory, this seems like a missed opportunity.

We thank the reviewer for this helpful suggestion and agree that the previous version of the Discussion did not sufficiently integrate earlier studies on Drosophila RH7. In the revised manuscript, we have expanded and restructured the discussion to explicitly incorporate key studies, including those by Ni et al. (2017), Senthilan et al. (2019), Lazopulo et al. (2019), and Meyerhof et al. (2024). In Discussion 5.4, we directly address similarities and discrepancies, such as differences in reported expression patterns, behavioral phenotypes, and experimental conditions. We use these inconsistencies to better position our findings and propose that RH7 acts as a modulatory photoreceptor with context dependent effects, which may explain the variability observed across studies. These changes provide a more integrated and coherent view of RH7 function.

(2) Similarly, the manuscript currently lacks a discussion of the possible relevance of rhodopsin7 (and other non-visual light receptors in other organisms) in the context of a species' environment and lifestyle, i.e., what is the relevance/benefit of having rhodopsin7 in the fly's everyday life?

We agree that the ecological relevance of RH7 deserved a more detailed discussion. According to the suggestion, we have now expanded the discussion to address the ecological and functional relevance of RH7 in the context of environmental light conditions and species-specific lifestyles (see Section 5.5). In particular, we now highlight that RH7 is frequently retained in species inhabiting sun-exposed environments and that its presence correlates with conditions of high light exposure, especially during early developmental stages. Together with our functional data in Drosophila, showing a role of RH7 in light dependent behavioral flexibility and circadian regulation, this supports the idea that RH7 contributes to the detection and integration of environmental light cues under natural conditions.

(3) An additional point concerns the title and abstract, which postulate rhodopsin7 roles in contrast vision as well as motion and brightness perception. Contrast remains poorly defined in the text, leaving it ambiguous whether it refers to bright/dark contrasts, e.g., along edges, or the temporal contrast that results from dark pulses (startle response). While the latter seems to apply here, the former is likely more intuitive. Thus, this aspect should be rephrased (also in the title) or properly clarified early on.

Thank you for this comment. We agree that the term “contrast” was ambiguous, as it can refer to spatial contrast (e.g., edge detection) or temporal contrast (changes in light intensity). Our study focuses on temporal contrast, such as light-dark transitions. Accordingly, we have revised the manuscript, replacing “contrast” with the more precise term “temporal changes in light intensity” throughout the relevant sections. In addition, to clarify this further, we conducted additional experiments with graded changes in illumination. These showed that Rh7⁰ mutants have reduced responses compared to wild type in both abrupt (e.g. 30→0 µW/cm²) and gradual (e.g. 30→5 µW/cm²) transitions, indicating that RH7 contributes to detecting temporal changes in light intensity.

(4) Regarding motion detection, this is backed up by the optomotor response results, but the findings stand somewhat isolated from the other results, lacking a clear connection aside from general visual processing.

We have clarified the connection between motion detection and the other visual assays. In the Results section (4.7), motion detection is now described as “relying on the processing of spatiotemporal changes in luminance across the visual field,” explicitly linking it to general luminance-based visual processing. In the Discussion (5.3), we added the concise statement “These computations rely on changes in light intensity over space and time” to further emphasize this connection. We believe these changes make the relationship between the optomotor results and the other assays clearer and easier to follow.

(5) Lastly, brightness perception is mentioned in the abstract, but never again, possibly due to inconsistent phrasing throughout the manuscript.

We agree that the terminology was not used consistently throughout the manuscript. To improve clarity and consistency, we replaced the term "brightness perception" in the Abstract with "temporal changes in luminance", which more accurately reflects the focus of our study.

Reviewer #2 (Public review):

(1) It is not that clear to me what rhodopsin does in terms of circadian regulation (even though its function might be circadianly regulated). The clear role in the light/dark distribution of activity might not be circadian per se, but mostly light/dark- driven and there is no evidence here for a role in the entrainment of the clock.

We thank the reviewer for this important point. We agree that our current data does not provide sufficient evidence for a direct role of RH7 in circadian regulation or clock entrainment. In this revision, we have examined LD (12:12) behavior in more detail and report changes in several activity parameters (Figure 3A). While these differences could in principle involve circadian mechanisms, our experiments do not allow us to distinguish between circadian effects and acute light-driven modulation of locomotor activity. We therefore present these results without interpreting them as evidence for a circadian function of RH7, and instead focus on light-driven behavioral effects under LD conditions.

(2) The authors should cite Lazopulo, which nicely shows that Rh7 has an important role in peripheral neurons to allow flies to escape from blue light (see below).

We thank the reviewer for pointing this out. We have now cited Lazopulo et al. (2019) at multiple relevant points in the manuscript, specifically regarding atypical RH7 expression in peripheral neurons, the functional effects of RH7 outside the LNvs, and its protective role in light-dependent behavior (discussion 5.1, 5.4, and 5.5). We believe these additions ensure that the manuscript accurately reflects the existing literature and appropriately acknowledges the contribution of Lazopulo et al. to understanding RH7 function.

(3) The finding showing that Galphaz but not Galphaq can trigger signaling from light-excited Rh7 is a very intriguing finding to better understand Rh7 function. Since Galphaz is related to Gi/o, it would be interesting to test those, for example, by expressing RNAi with Rh7gal4 and testing the Light-dark or light-off response behavior.

We agree that testing additional Gi/o-type Gα subunits would be highly informative for further dissecting RH7 signaling. However, in our preliminary experiments, RNAi-mediated knockdown of Rh7 itself did not result in a robust or statistically significant behavioral phenotype under our conditions. This is consistent with previous reports that RNAi in Drosophila can show variable efficiency and often results in incomplete knockdown, leading to weak or undetectable phenotypes (Dietzl et al., 2007; Green et al., 2014; Perkins et al., 2015). Given these limitations, we did not further pursue RNAi-based approaches targeting additional Gα subunits in the current study. Instead, we complemented our experimental findings with additional comparative and in silico analyses using FlyPredictome, which support a potential association between RH7 and Gi/o-type signaling components. These results have now been incorporated into the revised manuscript (Discussion 5.2). We agree that further functional validation of Gi/o-type G protein involvement, for example using genetic mutants, interaction assays or alternative approaches, would be an important direction for future studies.

(4) The change in the locomotor activity distribution between light and dark in LD conditions provides a nice assay for Rh7 function. Since Lazopulo et al. (2019) have shown that wildtype but not Rh7 mutants do escape from blue light, it would be important to compare and discuss these LD behavior data with the Lazopulo results. Precisely, is this nighttime preference linked to blue light?

To address this point, we conducted additional experiments, which are now included in the supplementary materials. Instead of the usual white light–dark (LD) cycles, we tested blue light–dark and green light–dark conditions. However, we observed only minor differences and no significant shift in light preference, as reported by Lazopulo et al. (2019). A likely explanation for this discrepancy is the difference in experimental light intensity. In our assays, we used moderate light intensities, approximately 30 µW/cm² for white light and 5–6 µW/cm² for color lights. Lazopulo et al. used substantially higher light intensities (2480 µW/cm² for white light and approximately 600 µW/cm² for colored lights). Even the higher intensities used in our arrhythmia experiments (~120 µW/cm²) remained well below those applied in their study.

Importantly, the behavioral paradigms differ: Lazopulo et al. assessed acute light preference/avoidance, whereas our experiments quantify locomotor activity distribution across the day under LD conditions. The latter is strongly shaped by circadian regulation and integrates multiple internal and external factors. Therefore, wavelength-dependent avoidance behavior observed under acute conditions may not directly translate into changes in daily activity patterns under moderate LD conditions. Although we cannot directly replicate the strong avoidance of blue light or preference for green light described by Lazopulo et al., our results do not contradict those of Lazopulo. The reduced activity during the midday phase in the wild-type flies, which is less pronounced in Rh7⁰, may suggest a potential protective function or preventive behavior in the WT flies. Since the moderate light intensities used in our LD assays are much less aversive, no strong wavelength-dependent preference was observed.

(5) However, the paper would be strongly reinforced by correlating this with the LD behavior. The LD phenotype should be tested in flies with Rh7 expression rescued under Rh7gal4 control (as done for the startle response). This is important to show whether the expression pattern is likely responsible for the described Rh7 function in LD.

We agree that assessing LD behavior in flies with Rh7 expression rescued under Rh7-Gal4 control is important to link expression pattern to function. We have now performed these experiments. The Rh7-Gal4–driven rescue results in a substantial recovery of the LD locomotor phenotype, bringing it closer to control levels than the UAS-empty condition. While the rescue does not fully reach wild-type levels, the observed trend and significant differences across specific parameters support a functional contribution of Rh7-expressing cells. These data are now included in Figure 5C and described in section 4.6.

(6) If L5 and or M11 drivers are available, they should be used to rescue Rh7? Since expression in some clock neurons is shown, the rescue experiment should also be done with a clock neuron driver.

Thank you for this helpful suggestion. We agree that cell type-specific rescue using L5- and/or Mi1 drivers, as well as clock neuron drivers, would be highly informative.

However, implementing these experiments is currently not straightforward. Targeting these neuronal populations requires the use of split-Gal4 driver lines, which can differ in expression strength and are therefore not quantitatively comparable across combinations. In addition, the required genotype would be highly complex: the two split-Gal4 components will be located on separate chromosomes, the UAS-Rh7 transgene is on another chromosome, and the Rh7⁰ mutation resides on the third chromosome. Combining all necessary elements in a single line would therefore require extensive genetic recombination. Importantly, we aim to avoid introducing mutations or markers on the X chromosome, as these are known to influence behavioral readouts. However, many of the available lines are in a white^- background, and assembling the full rescue genotype while maintaining a controlled genetic background across all chromosomes is therefore particularly challenging. For these reasons, we have not pursued these rescue experiments in the current study but consider them an important direction for future work.

(7) In the same line, can the LD phenotype (or startle response phenotype of Figure 4) be restored by expressing Rh7 under ppk control, as shown for the blue light avoidance phenotype by Lazopulo et al?

We thank the reviewer for this suggestion. However, in our experiments, we did not observe a blue-light avoidance phenotype comparable to that described by Lazopulo et al. (2019). Since this behavioral effect did not occur in our assay, we did not perform rescue experiments with ppk-regulated Rh7 expression. As previously discussed, the absence of pronounced blue light avoidance in our experimental setup is likely due to the moderate light intensities we used, which are significantly lower than those applied in Lazopulo et al.

Therefore, a ppk-mediated rescue would not be meaningful in our context.

(8) Finally, the Rh7 "darkfly" rescued flies should be tested in LD.

We agree that testing Rh7Darkfly rescue flies under LD conditions provides important insight into Rh7 function. We have now performed these experiments. The Rh7Darkfly rescue leads to a marked shift of the LD locomotor phenotype toward the Darkfly phenotype, with a stronger effect than observed in the Rh7 rescue lines. While the rescue does not fully recapitulate either wild-type or Darkfly controls, the observed trend supports a contribution of RH7 to the modulation of LD behavior in this genetic background. These data are now included in Figure 5C.

Reviewer #3 (Public review):

(1) The authors should clarify exactly what tissues were taken for the comparative qPCR. This is particularly interesting in terms of the retina. Since Rh7 appears not to be expressed within the photoreceptor cells of the retina, this raises the important question as to which cells it is expressed in. To address this important question, it would also be helpful to include an expression analysis of the retina itself (by extending the RH7-GFP expression patterns and/or adding HCR in situ of the ommatidia array). The cell types of the retina are very well classified, and some evidence already exists for Rh7 expression in support cells (e.g., Charlton-Perkins et al., (2017); PMID: 28562601). This study has a unique opportunity to investigate this further by adding these critical data for a more complete picture of Rh7.

We thank the reviewer for this helpful comment. We have now clarified in the Materials and Methods exactly which tissues were collected and analyzed for the comparative qPCR experiments. Regarding Rh7 expression in the retina, in our hands, we did not detect signals in retinal support cells, likely due to low expression and masking by autofluorescence. However, low Rh7 mRNA levels detected by qPCR in retinal tissue, together with the faint staining reported by Kistenpfennig et al. (2017), suggest that expression in these cells is possible. We have added this clarification, along with the observation by Lazopulo et al. (2019), who reported Rh7 expression in multidendritic neurons, to the Discussion (section 5.1) to provide a more complete overview of RH7 localization.

(2) Mammalian opsins should be included in the phylogenetic analysis illustrated in Figure 2A and indicate their position on the tree. This will allow readers to better put the authors' statements regarding the intermediate position of Rh7 into perspective. In addition, note that the distinction between red and deep red is easy to miss regarding the Rh7 cluster. Perhaps the authors could use a more distinct colour scheme, for example, orange and deep red.

In the revised Figure 2A, we have included both mammalian melanopsins and lophotrochozoan opsins, which support our interpretation of RH7 as a primitive opsin. The color scheme has been updated to more clearly distinguish the different clades, and tardigrades are now represented with a red triangle rather than a separate color. These changes improve clarity and better highlight the intermediate phylogenetic position of RH7.

(3) More details should be provided on the optomotor response experiments. Specifically, specifications of the frequencies used for the optomotor response are needed. Results show a relatively large level of variation, which may be due to different angular perspectives that flies may have had while viewing the stimulus. If possible, provide videos as examples, as they will make it clearer to viewers how much flies could move around in the setup (from the methods, it seems they could move within the 2.2 of the 3 cm diameter of the arena, which would lead to substantial differences in the visual angle of the viewed grating.

We would like to thank the reviewer for this valid point. We agree that, due to the relatively simple design of our optomotor apparatus, the flies may have different viewing angles of the rotating grid. To illustrate this point, we have added representative video footage and further photographs of the experimental setup to the supplementary material. A more sophisticated optomotor apparatus that maintains a fixed viewing angle for the animals would certainly reduce experimental variability. Nevertheless, our current, simple setup yielded robust and statistically significant optomotor responses. To further strengthen the robustness of these results, we have increased the sample size from n = 20 to n = 30, thereby confirming the observed effects.

Recommendations for the authors:

Reviewing Editor Comments:

(1) Claimed impact of rh7 on circadian regulation.

As the data are presented at the moment, there is no evidence for a role in circadian regulation. At present, the data can be fully explained by the acute effects of light on behavior. Either remove the circadian from the text or consider specific entrainment and rescue experiments (see suggestions from Reviewer 2).

We thank the editor for this important comment. We agree that the original version of the manuscript overinterpreted the role of RH7 in circadian regulation, and that the observed phenotypes can be explained by acute effects of light on locomotor behavior under LD conditions. In the revised manuscript, we have substantially restructured and clarified the interpretation of our findings. We now explicitly frame our results as light-driven behavioral effects under LD (12:12) conditions and have removed claims suggesting a direct role of RH7 in circadian entrainment. Furthermore, we have also added new rescue experiments, including Rh7-Gal4–driven Rh7 and Rh7Darkfly rescue, which provide further functional insight. These data show partial restoration of the locomotor phenotype and genotype-dependent shifts in activity patterns, supporting a modulatory role of RH7 in light-dependent behavior, while not directly addressing circadian clock function.

We have further revised the text to ensure that conclusions remain strictly aligned with the presented data. In addition, we now emphasize that our data provide a basis for future studies exploring the potential role of RH7 in circadian entrainment.

(2) Improved discussion section

Both Reviewers 1 and 2 point out several aspects that should be better taken care of, especially embedding the new results into the context of the existing literature on rh7- Lazopulo et al 2019, Ni et al 2017, Meyerhof et al 2024 were particularly mentioned.

We have addressed the reviewers’ suggestions by revising the Discussion section. We now refer to Meyerhof et al. (2024), Lazopulo et al. (2019), and Ni et al. (2017) at multiple points throughout the Discussion to better place our findings in the context of the existing literature on RH7 function. These references are now included in Sections 5.1, 5.4, and 5.5 of the Discussion.

(3) The addition of vertebrate melanopsins, as pointed out by Reviewer 3 (they suggest mammalian, but consider adding other vertebrate and also lophotrochzoan proteins), in the phylogenetic tree will help to put the evolutionary ancestrality claim into a better perspective.

We performed new bioinformatic analyses using RefSeq proteomes and carefully selected representative species across relevant clades to construct a balanced phylogenetic tree. These additions support our interpretation of RH7 as a primitive opsin and help place its intermediate phylogenetic position into better perspective. The results are presented in the revised Figure 2A, which now also includes mammalian melanopsins and lophotrochozoan opsins.

(4) There were several questions raised on the qPCR and optomotor response experiments (Reviewer 3), as well as the definition of contrast (Reviewer 1).

We have addressed the reviewers’ comments by substantially improving the clarity and presentation of the qPCR and optomotor response experiments, as well as the definition of “contrast.” We now provide a more detailed description of the qPCR analysis in the Methods section. For the optomotor response, we have added representative images and videos of the experimental setup to the Supplementary Material to increase transparency. We further clarified that the term “contrast” was previously used ambiguously and may refer to different concepts. In the revised manuscript, we now consistently refer to “temporal changes in light intensity” to specify that our study focuses on light-dark transitions. In addition, we included additional experiments with graded changes in illumination, which show reduced responses in Rh7 mutants compared to wild type under both abrupt and gradual transitions.

(5) Supplementary Material needs sorting

Accession numbers are in Supplementary File 2, not Supplementary File 1. Supplementary Material S2B is in Supplementary File 3 - this is really confusing. Supplementary Materials S3 is probably Supplementary File 1, and the phylogenetic tree shown there actually looks identical to the tree shown in Figure 2A of the main manuscript.

We sincerely apologize for the confusion regarding the Supplementary Material numbering and file assignments. This issue likely arose during the upload process or transfer from the bioRxiv version of the manuscript. We have now carefully checked and corrected the Supplementary Files to ensure that all accession numbers, figures, and files are correctly assigned and consistently labeled throughout the revised submission.

Reviewer #1 (Recommendations for the authors):

(1) Here, I will address specific aspects of the manuscript, elaborating on the points mentioned in the public review and also listing detailed suggestions.

As mentioned in the public review, the discussion could do a better job of relating the obtained findings to previous publications. For example, the paper by Ni et al. (2017) investigates the role of Drosophila rhodopsin7 in circadian light entrainment and its interplay with dcry, which seems relevant in the context of rhodopsin7 apparently being only present in CRY-negative clock neurons (except DN1a).

We thank the reviewer for this helpful suggestion. We have expanded the manuscript to further explore the potential relationship between RH7 and DCRY. Specifically, we performed additional bioinformatic analyses, which are now presented in Results Section 4.1, and in discussion sections 5.4 and 5.5 addressing this aspect. While previous observations by Ni et al. (2017) and Kistenpfennig et al. (2017) have already pointed to a possible relationship between RH7 and DCRY, our phylogenetic analyses provide additional support for such a connection from an evolutionary perspective. Although our data do not yet allow us to infer the precise functional nature of this relationship, they further strengthen the evidence that Rh7 and DCRY are evolutionarily and functionally linked.

(2) Another relevant paper by Meyerhof et al 2024 (doi:10.1073/pnas.2400964121) investigates the role of rhodopsin7 in shade preference and startle responses to short light pulses. The lack of shade preference and the altered startle response in rh7 mutants could be related to the authors' own findings on altered behavior in darkness. Further, the paper shows rh7 mutants to more rapidly return to baseline activity after a light pulse, which is somewhat reminiscent of the abrupt activity decrease in rh7 mutants at the start of the dark phase (18h). Generally, I recommend using the contradictory findings mentioned in the introduction as a starting point to describe where the new findings expand previous knowledge and possibly resolve contradictions.

We thank the reviewer for this suggestion. We have revised the Discussion to integrate our findings with the available literature, including the recent study by Meyerhof et al. (2024), and explicitly compare similarities and differences between the reported phenotypes and our own observations.

These aspects are now addressed in the newly added Section 5.5, where we discuss the evolutionary retention of RH7 in sun-exposed species and relate our phylogenetic findings to the emerging evidence that RH7 may play a conserved role in mediating responses to sun-exposed and shaded environments.

(3) One specific aspect that does not fully convince me is the interpretation of the behavioral patterns concerning the short photoperiods (Figure 3C). The authors state that rh7 mutants lose the flexibility to shift their activity into the dark phase. However, drawing a vertical line through panels A, B, and C, it rather seems that activity peak times in wildtypes are fixed to 6-7h and 17-18h, while rh7 mutants do actually shift their peak activities with the decreasing photoperiod. A way of quantifying this would be to determine the phase differences between M- and E-peaks. It may also help to align plots in a way so that lightson of long and short photoperiod plots align. There is clearly a difference between WTs and mutants, but I would be more careful in calling this a reduction in flexibility.

We thank the reviewer for this comment. We also noticed that the behavioral patterns under short photoperiods can be interpreted in different ways. Based on this comment, as well as the comments from the other reviewers and the handling editor, we decided not to further discuss the potential circadian component in this manuscript. We agree that additional and more targeted experiments will be necessary to better separate circadian effects from light-induced behavioral responses. These experiments are beyond the scope of the present study but will be important to further investigate the potential role of RH7 in circadian regulation. Therefore, we revised the manuscript to focus on the light-induced behavioral effects of RH7 and avoided drawing conclusions about circadian flexibility that are not yet fully supported by our data. In this process, we removed the data showing actvity under short days from the manuscript.

Below, I list individual points according to their line number in the manuscript:

(1) Line 1: Consider rephrasing the title based on the above comment regarding contrast.

We have revised the title accordingly.

The new title is: RHODOPSIN 7: An ancestral non-canonical photoreceptor shaping light-responsive behavior

(2) Line 10: Vision is also used to adapt to the environment, so maybe change to "...also to otherwise/indirectly adapt behavior...".

We have revised the sentence as suggested to clarify the non-image-forming role of light in behavioral adaptation.

“Animals rely on light not only for vision but also to adapt behavior to their environment through non-image-forming pathways.”

(3) Line 15: Consider rephrasing the title based on the above comment regarding contrast, motion, and brightness perception.

We thank the reviewer for this suggestion. The title has been revised accordingly. The new title is: RHODOPSIN 7: An ancestral non-canonical photoreceptor shaping light-responsive behavior.

(4) Lines 23-25: This reads as if light perception and vision are the same. Please clearly distinguish to make clear that vision is only one way in which light can be perceived and influence behavior.

We have revised the text to clarify that vision represents only one modality of light perception and that light can influence behavior via both visual and non-visual pathways. “The ability to detect and respond to light is fundamental for many organisms and can influence behavior through both visual and non-visual pathways. Vision relies on….”

(5) Lines 26-27: Here and also later in the introduction, it is hard to follow how different groups of opsin light receptors relate to each other (e.g., opsins (in general,) rhodopsins, r-opsins, c-opsins, non-visual opsins), etc.) This is also related to the fact that opsins can be differentially grouped based on phylogeny/structure (e.g., r- vs. c-opsins) or role/localization (e.g., visual vs. non-visual). Please revisit the introduction with a non-expert reader in mind, and try to address the groups hierarchically. In fact, a small tree-like figure of the different groups may be a simple solution.

We thank the reviewer for this helpful suggestion. We have revised the Introduction to simplify the presentation of opsin classification. c-Opsins and r-opsins are now introduced only briefly to place RH7 within the rhabdomeric opsin family. Since Drosophila contains only rhabdomeric opsins and these are the focus of our study, we did not further expand the Introduction with a detailed discussion of c-opsins or add a classification figure.

(6) Line 33: Please expand to "...image formation in the eye, some..." to be more precise. We have revised the sentence to clarify that rhodopsin-mediated image formation refers to visual systems.

“While the primary function of rhodopsins is image formation in visual systems, some are also known to participate in non-image-forming functions.”

(7) Lines 46-55: This detailed information about the different Drosophila rhodopsins is not referred to anywhere else in the manuscript. I suggest shortening and focusing on rh7.

We thank the reviewer for the suggestion. We have shortened the section to focus on RH7, as the other rhodopsins are not discussed elsewhere in the manuscript. The revised text now highlights the debated expression and potential function of RH7.

“Drosophila melanogaster (Dmel) has seven rhodopsins (RH1-RH7), all belonging to the ropsin group. While RH1–RH6 are expressed in well-characterized photoreceptors, the expression pattern and function of RH7 remain less clear and are still debated.”

(8) Line 55: The statement that the expression of Rh7 remains debated also occurs later in the introduction (line 88). If in line 55, it is about the expression sites specifically, references should be added. Otherwise, it may be sufficient to only address this aspect in line 88.

The statement in line 55 specifically refers to the expression sites of RH7. References to Ni et al., 2017 and Senthilan et al., 2019 have been added to support this point.

(9) Line 61: Which of these features distinguishes rhodopsins from other opsin groups?

We thank the reviewer for this comment. The RH7 section has been thoroughly revised to clarify both the features shared with other rhodopsins and those that distinguish RH7 from other opsin groups. Key distinguishing features, including the extended N- and C-terminal tails and the absence of the QAKKMNV motif in ICL3, are now highlighted at the beginning of the paragraph, while additional Drosophila-specific features, such as the palindromic RCSI, are discussed subsequently.

“RH7 displays the canonical rhodopsin features, including seven transmembrane helices, a chromophore-binding lysine, and the LRTPXN motif located in the first intracellular loop (ICL1)….”

(10) Figure 1: For panel B (left), please increase label sizes. For panel B (right), the color scale makes it very hard to see low-level expression (e.g., in Mi15 and below). Please try adjusting the color scale and/or consider only showing the cell types also indicated in the left part of the panel. For ninaE, please add "aka Rh1" or similar for the less informed reader.

We have revised Figure 1 accordingly. Specifically, we increased the label sizes in panel B (left) to improve readability. For panel B (right), we adjusted the color scale to better visualize low-level expression and improve overall clarity. In addition, we updated the labeling of ninaE to “Rh1 (ninaE)” to aid accessibility for a broader audience.

(11) Lines 88-90: What exactly were the contradictions that emerged from previous studies? Also see the comment in the public review regarding the discussion of the results.

Thank you for pointing this out. We have clarified this in the revised manuscript. “Previous studies on RH7 have yielded conflicting results regarding its function and expression, including discrepancies in the identified neuronal populations and associated behavioral phenotypes”

(12) Line 91: Briefly explain the characteristics of white and yellow mutations so the reader can assess why these are relevant here.

We have clarified the role of the white and yellow genes in the genetic background. The revised text now reads:

“Both genes are expressed in the optic system (Davis et al., 2020; Supplementary Material) and are known to affect neuronal function and behavior (Bond et al., 2024; Drapeau et al., 2003; Rickle et al., 2025).”

In addition, we have visualized the expression data for yellow and white from Davis et al. in the Supplementary Material for more clarity.

(13) Lines 100-101: Circadian entrainment is not a typical visual function. Please rephrase.

The sentence has been revised for clarity and now reads:

“As an ancestral rhodopsin, RH7 appears to contribute to basic visual functions, such as contrast processing, as well as to non-visual functions like circadian synchronization, similar to melanopsins in mammals.”

(14) Line 105: The exact address is not necessary, mention BLASTP is enough.

Thank you. We have now removed the exact address and we now simply refer to BLASTP.

(15) Line 108-109: If default settings were used, the details are not needed.

We have omitted the details, as they are not necessary.

(16) Line 113: These settings seem to repeat line 108. Needed?

We thank the reviewer for pointing this out. In the original version, the settings in line 108 referred to the BLAST search, while those in line 113 pertained to the phylogenetic tree, where the parameters are essential, because phylogenetic inference depends on dataset- and method-specific choices. However, this entire section has now been revised, as the phylogenetic tree has been completely rebuilt with a much broader dataset, including mammalian melanopsins and lophotrochoan r-opsins.

(17) Line 122: Without further context, these abbreviations are non-informative and confusing to many readers. Provide details or rephrase. The same applies to DMEM, FBS, and Glo22F in the same paragraph. While many readers will understand instantly, keep the diverse audience of eLife in mind.

We have now added explanations for all abbreviations in the paragraph to improve clarity for a broad audience. Specifically, the Gα subunits (GNAS, GNAL, GNAQ, GNA11, GNA12, GNA13, GNAZ) are now clearly defined, and DMEM, FBS, and Glo22F are also explained as Dulbecco’s Modified Eagle Medium, fetal bovine serum, and a cAMP-sensitive luciferase reporter, respectively. These changes should make the methods clearer and more accessible to all readers.

(18) Line 144: "constant conditions" is not ideal as it could be misinterpreted as DD or LL. Please rephrase.

We agree with the reviewer and have removed the phrase “constant conditions” to avoid potential misinterpretation.

“All recordings were performed under 60% relative humidity and 25 °C…”

(19) Line 148: Stating Lux values for Drosophila is not informative as the unit is based on the spectral sensitivity of the human eye. Ideally, provide a spectrum of the used light source as a supplement.

We thank the reviewer for this suggestion. We agree that lux values alone are not informative for Drosophila, and we have now included the spectrum of the light source in Figure 3–figure supplement 1A.

“A standard day was defined as 12 h light (30 µW/cm² ~ 100 lux, the spectrum of the light is shown in Figure 3–figure supplement 1A) and 12 h darkness”. In addition, to ensure complete consistency of the experimental conditions, we repeated some earlier experiments using the same light source as in the rest of the study, since the exact light source used in the initial experiments could no longer be verified. This ensures that all behavioral experiments presented in the revised manuscript were performed using the same light source.

(20) Lines 149-153: The startle response protocol is hard to understand when only reading it. It could help to state when (relative to lights-on) the first dark pulse was given and how many dark pulses were given per light phase.

We have clarified the timing and frequency of the dark pulses in the Methods section. We now specify that the first dark pulse was applied 1.5 h after lights-on and that six dark pulses were delivered during each 12 h light phase.

(21) Lines 159ff: The 4-hour startle response assay is not clearly distinguished from the previously mentioned assay (30 min D + 1.5h L). I could help to start with e.g., "In a second assay..." and to clearly state why this additional assay was performed. That is, what information can the 4-hour assay provide that the previous assay could not?

We have revised the text to clearly introduce the 4-hour startle response assay as a second, distinct paradigm (“In a second startle response assay…”).

We also clarified its purpose: in contrast to the initial assay, this paradigm was designed to measure the acute startle response independently of circadian influences. To this end, flies were rendered arrhythmic and exposed to repeated 4-hour light–dark cycles, preventing re-entrainment and isolating the startle response.

In addition, we now refer to a schematic of the light regime in Figure 3–figure supplement 1C.

(22) Lines 161-163: As flies were kept in LL aside from the dark pulses, it could be more intuitive to talk about 72h or three 24h intervals rather than 3 days. Otherwise, one might assume that the initial constant light was followed by 3 days of LD plus dark pulses.

We have revised the text to emphasize the total duration (“72 h”) to avoid confusion with a 24-hour LD regime. In addition, we now provide a schematic of the light regime in the Supplementary Material (Figure 3–figure supplement 1C).

(23) Line 172: Please write out CantonS once, as otherwise it only occurs in Table 1. Also, clarify that y+ and w+ refer to the (absence of the) yellow and white mutation, respectively.

We have revised the text to write out Canton-S (CS) upon first mention and clarified that y⁺ and w⁺ denote wild-type alleles of the yellow and white genes, respectively, meaning any mutations in these genes are absent.

(24) Table 1: Consider adding "(truncated RHSOPSIN7)" or similar to the "Darkfly" cell.

We have updated Table 1 to indicate that the Darkfly line carries a truncated RH7. The description now reads: “This line has been maintained for decades in constant darkness and carries numerous mutations, including a truncated RH7 lacking the last 21 amino acids.”

(25) Table 2: In the formatted paper, Table 2 should appear after section 3.5 so the reader can properly interpret the applications and names.

We have placed Table 2 immediately after section 3.5 as suggested.

(26) Table 3: Consider adding the product IDs of the used antibodies for convenience.

We have added the product IDs of all antibodies used to Table 3 for convenience.

(27) Lines 180ff: This section should initially state the purpose of establishing the rh7-Gal4 line, i.e., the expression of selected gene in rh7-expressing cells. Again, keep your (lee-informed) readers in mind.

We have revised the section to clarify the purpose and design of the Rh7-Gal4 line. It now states that the line was generated to identify Rh7-expressing cells and explains the use of a relatively large promoter region including exon 1 and 2.

(28) Line 190 w1118 flies do not occur in Table 1. While used by a commercial company here, please still include them for completeness.

We have added the w¹¹¹⁸ line to Table 1 for completeness, as well as the BDSC Stock #8621 line, which was used as the background for the UAS-construct flies.

(29) Lines 192ff and 203ff: As for lines 180ff, start with a brief description of what the purpose of the respective works was.

We have revised the section to start with a brief description of the purpose of the rescue experiments. The text now clearly states that UAS constructs were generated to assess the ability of different Rh7 variants to rescue the phenotype, with UAS-Rh7 as the wild-type rescue, UAS-Rh7^Darkfly carrying the Darkfly variant, and UAS-empty serving as a control. We have added an introductory sentence to the optomotor section in Materials & Methods to clarify the purpose of the experiments: “To investigate the contribution of Rh7 in the lamina and medulla to visual motion detection, male flies were individually tested for their optomotor walking behavior.” This makes clear why the assay was performed before describing the setup and measurements.

(30) Line 225: Just to be safe, make sure to not mix up Δ-CT and 2-ΔΔCT (see Livak & Schmittgen 2001, doi: 10.1006/meth.2001.1262).

We confirm that ΔCT was indeed used to calculate relative mRNA levels. To clarify this, we have now added the formula to the text: ΔCT = CT_α-tubulin − CT_Rh7.

(31) Line 229: Please state the light (cycle) conditions under which the flies were raised, as well as the sampling times at which they were fixed.

We have now specified the light cycle conditions under which the flies were raised (12 h light:12 h dark at 25 °C) in the Methods section. For qPCR experiments, tissues (retina, lamina, and brain) were carefully dissected from adult flies without prior fixation to preserve RNA integrity. Dissections were performed during the light phase and were not restricted to specific time points. These details have been added to the revised manuscript (section 3.10).

(33) Lines 296-297: This brief description could go at the start of section 3.2.

The sentence describing the GsX assay (“To test the functionality of RH7, we used a GsX assay designed to determine which Gα proteins can bind to a given GPCR, in this case RH7 (Ballister et al., 2018)”) has been moved to the Methods section (now 3.3) as a brief introduction to the approach.

(34) Line 305: Clarify that 2 different retinals were tested.

We clarified that two different retinals were tested. The text now reads: “We observed robust activation with the Gαz chimera, with both 9-cis-retinal and all-trans-retinal (Figure 2C).”

(35) Figure 2A, B: I suggest using a different color for the RH3,4,5, branch for better distinction from RH7.

We have generated a new tree and adjusted the branch colors to improve clarity between RH3,4,5, branch and RH7.

(36) See comment above regarding the shifting/flexibility of WTs vs. rh7 mutants.

Following the reviewers and editor's recommendations, we revised the manuscript to focus on the light-dependent effects of RH7 and no longer interpret our data in terms of shifting ability or circadian flexibility. The corresponding statements have been removed or revised accordingly.

(37) Line 348: Please change "occur" to "be triggered".

The wording has been updated as suggested, replacing “occur” with “be triggered” in the text.

(38) Line 355: I would mention the double mutants only after the results from the rh7 single mutants were described.

We have adjusted the order of the text accordingly and now introduce the double mutants only after describing the Rh7 single mutants.

(39) Line 362: See comment on line 159ff.

We have added a sentence at the beginning of the section to clearly introduce the 4-hour startle response assay as a second, distinct paradigm: “In a second startle response assay (4-hour assay), designed to measure the acute response independently of circadian influences…” This clarifies its purpose and distinguishes it from the initial assay.

(40) Line 368: Write "rh7 mRNA" to be precise.

We have updated the text to use “Rh7 mRNA” for precision, as suggested.

(41) Figure 5: If possible, please sort the panels in the order in which they are mentioned in the text. For panel E (right), the orientation of the lower schematic, relative to the upper one and the left panel, is unclear. Is it possible to add orientation indicators? Alternatively, could L5 and Mi1 neurons be indicated in the upper schematic instead?

We thank the reviewer’s helpful suggestion. Since reorganizing the figure panels was challenging and would have affected the overall layout, we instead revised the corresponding text to ensure that the order of panel descriptions matches the figure arrangement. To address the concern regarding panel E, we have added orientation indicators to the schematic to clarify the relative positioning.

(42) 419 Add "A)".

We have added an A).

(43) Line 432: Later on (line 598), it is mentioned that the other accumulated mutations in Darkfly may also have affected the observed patterns. Are there any specific mutations worth highlighting in this context aside from rh7?

We thank the reviewer for this comment. In response, we have expanded the Discussion to highlight additional mutations in the Darkfly genome that may contribute to the observed phenotype. Nonsense mutations in HisCl1 and Vha100-1 could affect visual processing and neuronal signaling, potentially altering sensory input and synaptic function. Missense mutations in DopR, bgm, and developmental regulators such as Sox21b may further modulate activity, sleep, and neural development. We have updated the Discussion accordingly to make these points clear.

(44) Lines 435-436: Unchanged mRNA levels do not necessarily equal the presence of the translated protein. Is there another way to properly confirm this? E.g., rh7 HCR in Darkfly?

We agree that unchanged mRNA levels alone do not confirm the presence of translated protein. While in situ HCR does not directly measure protein levels, it provides additional information on the cellular localization and presence of Rh7 transcripts beyond qPCR measurements. We have therefore performed Rh7 in situ in Darkfly and included this data in Figure 5—figure supplement 1B.

(45) Line 439: "activity" is too vague based on only the altered dark pulse response. I would rather suggest factors like increased protein concentrations/stability, increased sensitivity, constitutive activation, etc.

By “activity,” we refer to the molecular activity of RHODOPSIN 7 as reflected in the behavioral response. The Results have been revised to:

“When we exposed the Darkfly to dark pulses in a 12:12 light-dark cycle, they exhibited the opposite phenotype to Rh7⁰ mutants, showing a stronger startle response (Figure 6A), possibly reflecting RHODOPSIN 7 adopting a constitutively active form in the Darkfly strain, driving the enhanced behavioral response.”

(46) Lines 442-446: The no-rescue control does not fully resemble WTs as they lack the gradual activity decrease after lights-off. The abrupt decrease (also in the 2 rescues) is more reminiscent of the rh7 mutants. This could be discussed in the context of what was mentioned at the start of this section (Meyerhof et al 2024 paper).

We agree that the rescue lines do not fully restore all aspects of the WT control locomotor pattern. One possible explanation is that the Rh7-Gal4 driver does not fully represent the endogenous Rh7 expression pattern. As described in the Results section, our in situ hybridization analysis identified additional Rh7-expressing cells, particularly in the optic system, that were not detected by the Rh7-Gal4 line (results, section 4.5). We have added this point to the Discussion to address how the broader Rh7 expression pattern may contribute to the observed behavioral effects (discussion 5.4).

(47) Line 472: "restored the reduced startle response" reads a bit convoluted. Better write e.g., "restored the enhanced startle response that was absent in the no-rescue mutants".

We have revised the text as suggested to clarify the phrasing.

(48) Lines 533-535: Please provide a reference for the statements about L5 and Mi1 functional roles. Also, this is the only part where there is some connection made between rh7 (expressed in Mi1) and contrast processing (which involves Mi1). As this is a rather weak connection, please consider the last paragraph of the public review section.

We have added references to support the functional roles of L5 and Mi1 neurons. L5 neurons relay signals from outer photoreceptors to the medulla and show strong contrast adaptation (Matulis et al., 2020). Mi1 neurons contribute to motion and contrast processing (Behnia et al., 2014; Matulis et al., 2020). To address the connection between Rh7 expression and contrast processing, we have carefully phrased the text to indicate a potential role of Rh7 in modulating contrast-related signals in Mi1, while noting that the functional link remains to be directly tested. We believe this wording, together with the added references, provides proper support for the statements and maintains a cautious interpretation.

If contrast perception shall indeed be investigated, this may be done by performing the optomotor assay with gray stripes of different contrast, with stripes where the edges are not sharp but show a gradual change from black to white.

We agree that contrast perception can be assessed in more detail using stimuli with defined contrast levels and gradual luminance transitions. However, our aim was not to directly measure contrast sensitivity, but rather to investigate behavioral responses to changes in luminance. We have clarified this distinction in the revised manuscript and now specify that the optomotor response reflects processing of spatial and temporal changes in luminance, while the light-off startle response measures responses to abrupt changes in luminance.”

(49) Lines 546-547: Are there references on how activity or behavior in general can affect external light cues?

We have added appropriate references to support this statement. In particular, we now cite Rieger et al. (2003), which demonstrates direct effects of light on locomotor activity (masking), and Helfrich-Förster (2017), which provides a comprehensive overview of circadian regulation and light-dependent behavioral modulation. These additions clarify how external light cues can directly influence behavior in addition to circadian clock control.

(50) Lines 557-560: See comment above regarding the shifting/flexibility of WTs vs. rh7 mutants.

We thank the reviewer for this comment. We agree that assessing shifting and behavioral flexibility would require dedicated experiments, such as jet lag or entrainment assays. We have therefore revised the focus of the manuscript and now primarily discuss RH7 function in light-dependent behavioral responses rather than broader flexibility of the circadian system. Future studies will further explore the potential contribution of RH7 to behavioral adaptation and flexibility using dedicated experimental approaches.

(47) Lines 564-567: How many species possess dcry but not rh7? This is an important distinction, as otherwise one could assume that both must always co-occur. Alone, this provides only limited support for a potential functional interplay. The findings by Ni et al. (2017) regarding dcry and rh7 in entrainment could, however, help strengthen this point.

We have clarified the evolutionary relationship between DCRY and RH7 in the revised manuscript. We now specify that, although DCRY is widespread across Bilateral and many non-panarthropod species possess DCRY without RH7, RH7 and DCRY show a strong evolutionary association within arthropods, with approximately 98% of DCRY-retaining arthropod species also retaining RH7. At the same time, the presence of RH7 in some lineages lacking DCRY suggests that RH7 may retain functional relevance in the absence of DCRY. Together with previous findings on the functional interaction between RH7 and DCRY in light adaptation (Ni et al., 2017), these evolutionary patterns support a conserved connection between the two light-sensing systems, while the exact nature of this relationship remains to be further investigated. These points are now shown and discussed in section 4.1 and 5.5.

(48) Lines 579-580: Here, one could explicitly mention that this is supported by the lack of diel startle response modulation in the per mutants (Figure 4A).

We have modified the text to explicitly highlight this point. The sentence now reads: “Dark-pulse experiments show that both wild-type controls and per⁰ mutants, which lack a functional circadian clock, exhibit a strong startle response, consistent with the absence of diel modulation of the response in per0 mutants (Figure 4A).”

(49) Lines 596-597: The increased night activity in Darkfly seems largely limited to the first half of the night (compare e.g. Figure 6A and Figure 3A). Again, the loss/alteration of rh7 seems to have its major effect after a transition from light to dark (see lines 442-446, start of the section).

We thank the reviewer for pointing out this issue. The wording in the previous version could have been misleading. By “dark phase,” we meant the 30-minute periods without lighting during the dark-stimulus experiments, and not the “night phase.” We have revised the text to clearly refer to the startle response.

We also clarify that the increased locomotor activity observed in the “Darkfly” strain outside of the startle response is likely caused by additional background mutations that accumulated during long-term rearing in constant darkness, and not exclusively by the RH7 deletion.

(50) Line 622: See comments regarding contrast and motion perception. Do the N- and Cterminal regions of RH7 and melanopsin share similarities in sequence or additional characteristics aside from phosphorylation sites? This could support a conserved role.

We thank the reviewer for this suggestion, which prompted us to perform a more detailed analysis of conserved features between RH7 and melanopsins. In addition to the extended and potentially highly phosphorylatable N- and C-terminal regions, we identified several conserved sequence motifs, including two in the C-terminal region and others within the transmembrane core. One of these motifs extends into the conserved DRY motif in the second intracellular loop (ICL2). These findings are now described in the Discussion (section 5.7) to highlight potential structural similarities beyond phosphorylation sites. The corresponding sequence alignments are provided in the supplementary material.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Hu et al. investigated the role of olfactory ErbB4 in regulating olfactory information processing. The authors demonstrated that ErbB4 deletion impairs odor discrimination, sensitivity, habituation, and dishabituation by using an impressive combination of techniques from morphological to electrophysiology (both slice and in vivo) and from viral injection to cell-type-specific mutation to behavioral analysis. The findings underscore the crucial role of ErbB4 in olfactory PV neurons in modulating mitral cell function and odor perception.

Strengths:

This study contains a pretty comprehensive set of experiments.

Major concerns:

(1) Line 151 page 7, "PV-Erbb4+/+ mice (generated by crossing PV-Cre mice (Wen et al., 2010) with loxP-flanked Erbb4 mice". Does this mean mice carrying PV-Cre and ErbB4 floxed allele? Or with the WT allele? This is confusing. Figures 2B and 2C, ErbB4 expression was evident in many cells that were not positive for PV. What are the identities of those cells? Are they important?

Thank you for your positive comments regarding our study. PV-Erbb4^+/+ mice carried the PV-Cre transgene with the WT allele. In the revised manuscript, we have simplified the description of the genotype for clarity and have provided detailed breeding information in the "Materials and Methods" section (Line 532).

As shown in Figures 2B and 2C, ErbB4 expression was evident in GL and GCL cells that were not positive for PV. The activation of ErbB4-expressing cells in the GL and GCL has been suggested to upregulate theta and gamma oscillations, respectively (PMID:35853717). Mammalian OB are the most abundant and varied interneurons among brain tissues, and their functional importance and diversity remain unclear (PMID:31358754 and PMID:32208366). ErbB4-expressing PV interneurons in the EPL and IPL were relatively less abundant but accounted for the majority of inhibitory inputs to M/TCs. Importantly, one PV interneuron connects with over 1000 M/TCs to mediate recurrent and lateral inhibition, linearly controlling the OB output (PMID:31358754 and PMID:39186804). This study provides evidence that ErbB4 signalling in PV interneurons is required for olfactory discrimination and dishabituation.

(2) In Figure 4, the authors performed tetrode recordings in awake head-fixed animals. Although individual neuron spikes could be obtained by spike-sorting, this is not a "single-unit" experiment due to the nature of this approach.

What is the odor used in Figure 4? How did the authors clean up the odor to limit the stimulation within 2 seconds? In what layer were the tetrodes placed? What is the putative cell type presented in Figure 4C? If Figure 4C is a representative neuron recorded, the odor-induced suppression of spike activity seems to be impaired in PV-ErbB4-/- animals. However, Figure 4D shows that suppressed neurons were similar between the two types of animals. Such comparisons among individual mice are difficult for in vivo electrophysiological experiments because the recorded cell type and placement of electrodes would be different. The authors should apply ErbB4 inhibitors to the same animals and compare the effects before and after. This would ensure the recording of the same population of neurons.

Thank you for your valuable comment and suggestion. We agree that tetrode recording combined with spike-sorting is not a strict "single-unit" approach, although this method is widely accepted and consistently referred to as "single-unit recording" even "single-neuron recording" (PMID:30833706). Based on your comments, we modified the description as follows: “To obtain individual neuron spikes, units were identified by principal-component analysis scan (PCA) clustering of the spikes” (Lines 210-212).

As shown in Figure 4, a standardised panel with eight tubes delivers eight odours: isoamyl acetate, 2-heptanone, phenyl acetate, benzaldehyde, dimethylbutyric acid, n-heptanoic acid, n-pentanol, and 2-pentanone. Odours were delivered via an odour delivery system (Thinkerbiotech), and charcoal-filtered air was supplied to the mouse’s nose at a constant rate of 1 L/min to eliminate airflow interference, which effectively limited the stimulation to 2s. We have added the above description to the revised "Materials and Methods" section (Lines 786-789).

Author response image 1.

The tetrodes were placed within the ventral mitral cell layer based on stereotaxic coordinates. The putative cell type is mitral/tufted (Figure 4C). Despite the presence of diverse cell types in the OB, only the spiking activity of M/TCs can be captured via tetrode recordings (Kay and Laurent, 1999; Doucette et al., 2011). We added the above description in the revised "Materials and Methods" section (Lines 764-767). As you have indicated, Figure 4C shows the impairment of odour-induced spike suppression in PV-Erbb4^-/- mice. Consistently, Figure 4D shows the decreased suppression of odour-induced spike activity in blue (quantified in Figure 4I ΔMFR, ~25%), but the increased number of suppressed neurones in the PV-Erbb4^-/- group (Figure 4L). Considering that applying ErbB4 inhibitors to the same animals has no selectivity for blocking ErbB4 signalling in PV interneurons, in vivo neural signals typically drift over time when performing pre- and post-inhibition comparisons. Therefore, we compared in vivo electrophysiological data at the population level according to previous studies (PMID: 35173173, PMID:28425486, and PMID:28817803).

(3) At a glance in the heatmap in Figure 4D, excited neurons were reduced in PV-ErbB4-/- mice, but not inhibited neurons. This was different from Figure 4L. The authors need to have a criteria or threshold to show how they categorized each population.

In Figure 4L, red denotes excited neurones, whose number decreased from 66 to 16 in the PV-Erbb4^-/- group, and blue denotes inhibitory neurones, whose number increased from 81 to 148 in the PV-Erbb4^-/- group. This trend is consistent with that observed in Figure 4D. The classification criteria for each population were defined as follows:

“To determine whether the odour evoked a significant response, we used the Wilcoxon signed-rank test to compare the spontaneous (baseline) firing rate and odour-evoked firing rate of each unit–odour pair across all trials; unit–odour pairs with P > 0.05 were defined as nonresponsive, those with P < 0.05 as responsive, and responsive pairs were further categorised as excitatory (odour-evoked firing rate > spontaneous firing rate) or inhibitory (odour-evoked firing rate < spontaneous firing rate). Details are provided in the "Off-line spike sorting and statistics of the unit data" section of Materials and Methods (Lines 810-816).

(4) Figure 4D, 4F and 4J seemed to be inconsistent. In Figure 4D before odor, there was no clear increase in the spontaneous activity in PV-ErbB4-/- mice; in Figure 4F-4G and 4J-4K, clearly, there was a high spontaneous activity in PV-ErbB4-/- mice.

Figure 4D, 4F and 4H shows odour-evoked changes in mean firing rate (ΔMFR), calculated by subtracting the baseline firing rate. By contrast, Figures 4G and 4I show raw spontaneous mean firing rate (MFR), which was elevated in PV-Erbb4^-/- mice. We have revised the description of Figure 4D in both the Results section (Line 222) and figure legends (Line 1217).

(5) What are the neurons recorded in Figure 6E-6F? If they were MCs, loss of ErbB4 in PV neurons should not alter their intrinsic electrical properties. Rather GABAergic inputs could be altered. Indeed, the authors presented a reduction of GABAergic inputs from PV neurons to MCs.

The neurones recorded in Figures 6E-6F are indeed mitral cells (MCs). The firing frequency of action potentials reflects not only the intrinsic electrical properties but also the balance between excitatory and inhibitory synaptic inputs. As demonstrated in this study, the loss of ErbB4 in PV neurones leads to reduced GABAergic synaptic inputs from PV interneurons to MCs, which is consistent with our reasoning and is a key factor contributing to the observed changes in the action potential firing of MCs

(6) Figure 8E-8H, a better experiment would be specifically expressing ErbB4 or PV neurons. In Figure 8F and Figure 8I, was it the excitability after the current injection? Why not perform the spontaneous activity recording?

According to your suggestion, we used optogenetics to activate PV interneurons and recorded inhibitory postsynaptic currents (IPSCs) in MCs. As shown in the revised Figure 9 and Supplementary Figure 1F and 1G, deleting ErbB4 of PV interneurons in the OB weakened the inhibitory modulation of MCs by PV interneurons.

Figures 8F and 8I show the excitability after current injection. We did not measure spontaneous activity, primarily because the spontaneous firing frequency varies significantly among different cells, resulting in poor stability. In contrast, current-injection-induced excitability is more stable and quantifiable, making it more suitable for assessing specific changes in MC responsiveness caused by altered PV-MC inhibitory inputs.

Reviewer #2 (Public review):

Summary:

Hu et al investigate the role of PV neurons and their expression of Erbb4 in olfactory performance through a series of behavioral tests, selective knockout experiments, and in vivo and in vitro electrophysiology. Knockout of Erbb4, either in PV cells or the whole OB, resulted in impairment of discriminating complex odors. The authors present data that inhibition is impaired in MCs, which is likely underlying the abnormal odor-evoked responses of MCs in vivo and the impaired behavioral responses.

Strengths:

Overall, a key strength of this manuscript is the breadth of experiments to test the role of PV Erbb4 expression on circuit dynamics and behavior. The behavioral experiments were clear and sufficiently powered.

Weaknesses:

The major drawback of this manuscript is the lack of depth and rigor in experiments. Some experiments are preliminary, underpowered, and not quantified. As a result, many conclusions of the manuscript are weakly supported in its current form and would require significant revisions to address these shortcomings. Major weaknesses that should be addressed are as follows:

(1) AAV-PV-Cre-GFP is not described or validated. Is this the S5E2 enhancer or something else? What is the specificity and efficacy of this approach in selectively knocking out Erbb4 in PV neurons? Reduced Erbb4 expression in the entire OB with PCR does not validate the selectivity of this approach. At a titer of 10^12, it is unlikely to be specific. Even a small amount of off-target Cre expression will knock out the gene in non-PV cells, so the authors should show whether the gene is knocked out at the single-cell level from PV and non-PC cells. Without validation of this approach, this experiment is no different than the AAV-Cre-GFP experiments.

Thank you for your comment and thoughtful suggestion. The AAV-PV-Cre vector used in this study was purchased from BrainVTA (catalogue number: PT-0275; vector name: rAAV-fPV-CRE-bGH polyA), which contains an fPV promoter to ensure the selectivity and a β-globin intron to enhance Cre expression efficiency. Importantly, the specificity and efficacy of this AAV-PV-Cre construct in selectively targeting PV-expressing neurones have been validated in multiple published studies (PMID:40196908 and PMID:31987494). According to your suggestions, we also performed immunofluorescence staining (co-staining for PV and ErbB4) and found that ErbB4 expression was specifically reduced in PV-positive interneurons in OB tissues injected with AAV-PV-Cre, while ErbB4 levels remained unchanged in PV-negative cells (the revised Figures 9B and 9C). This single-cell-level validation directly demonstrated that our AAV-PV-Cre-mediated knockout approach specifically targets ErbB4 in OB PV interneurons, thereby avoiding off-target effects in non-PV cells.

(2) Figure 1D - three mice per group is insufficient. There is no control group error (the same as Figure 9). Why is it a paired t-test when there is a control group? The authors should be comparing go/go vs. go/no-go. The methods for normalization are unclear and are likely to hide the fact that n=3 is insufficient to capture a difference without extra measures to normalize the data.

Thank you for the comment. According to your suggestions, we expanded the sample size to four mice per group and modified the statistical test from a paired t-test to an unpaired t-test in the revised Figure 1C and 1D. Since not all samples were exposed to the same blot for direct comparison, we performed normalisation of each sample relative to its internal control prior to statistical analysis to ensure the reliability of group comparisons. There was an error regarding the control group in the revised Figure 1D. Detailed information on the normalisation method and updated statistical results have been provided in the revised figure legends (Lines 1116-1118).

(3) The analysis of LFP is limited. During what period was this quantified? Are there any differences in task-related LFP changes? Also related to in vivo electrophysiology, the authors should show examples of isolated units, including their waveforms and how units were clustered and assigned to M/TCs.

Thank you for the comment. The spectral power of each frequency band was quantified using a 4-s sliding window during the pre-odour stimulation period (4–0 s before odour onset). Regarding task-related LFP changes, the initial recordings were affected by unavoidable interference, leading to unstable signals that precluded reliable analyses. Based on your suggestions, we have supplemented the revised manuscript with examples of isolated single units, including their representative waveforms, clustering results (e.g. principal component analysis plots), and unit assignment criteria (the revised Figure 4—figures supplement 1A and 1B). As previously noted, the tetrodes were placed in the mitral cell layer based on stereotaxic coordinates. Consistent with established literature (Kay and Laurent, 1999; Doucette et al., 2011), the putative cell type recorded using this approach was mitral/tufted cells (M/TCs). Detailed methodological parameters for spike sorting, unit isolation, and cell type identification are provided in the "Materials and Methods" section (Lines 764-767 and Lines 803-805).

(4) The authors use 80pA and 100pA to elicit equivalent AP spiking in MCs to determine if recurrent inhibition differs, but do not actually show that AP spiking is the same across groups. This should be quantified.

There seems to be a prominent increase in the firing of MCs in PV-Erbb4+/+ mice before odor presentation, but not in PV-Erbb4-/- mice. What is the significance of this?

Thank you for your valuable comment and suggestion. According to your suggestions, we quantified the AP firing frequency of MCs in both groups under the respective stimulation currents, and statistical analysis confirmed that there was no significant difference in the AP spiking levels between the two groups (the revised Figure 8—figure supplement 1A).

We speculate this prominent pre-odour firing increase in PV-Erbb4^+/+ mice (but not in PV-Erbb4^−/− mice) stems from interference caused by the opening of the solenoid valve during odour clearance prior to stimulation—this artefact was present in the initial recordings of control mice but was eliminated during the data acquisition for PV-Erbb4^−/− mice. This was not statistically significant. To avoid this interference, we strictly defined the analysis windows, and the spontaneous firing rate was calculated by averaging the spikes recorded during the 4–2 s period before odour stimulation, excluding the interference-prone interval immediately before odour onset. This rigorous window selection ensured the reliability of our comparisons of spontaneous and odour-evoked firing between the groups.

(5)There is a disconnect between the in vivo firing rates of MCs and ex vivo firing rates. In slice, the authors note that the spontaneous activity of MCs is elevated in the KO, but this is not observed in vivo, where conditions are physiological. Therefore, it is unclear whether the concept of signal-to-noise changes in slice (higher spontaneous, lower evoked), indeed translate to something in vivo. It would be important to know what the PV cells are doing in vivo. Perhaps they have low firing rates prior to odor onset, which may explain the lack of observed difference in baseline FRs in MCs. The authors should have this data in their tetrode recordings, which would offer insight into when inhibition is recruited.

Thank you for your valuable comments, which helped clarify the consistency between in vivo and ex vivo electrophysiological data. In ex vivo slice recordings, we measured both spontaneous and evoked excitatory firing rates of MCs, and found that the spontaneous activity of MCs was elevated in PV-Erbb4^−/− mice (Figures 6A and 6B). Importantly, this observation is consistent with our in vivo data: M/TCs in PV-Erbb4^−/− mice exhibited significantly higher spontaneous firing rates during excitatory responses to odour presentation (Figures 4F and 4G). However, for inhibitory responses during odour presentation, M/TCs in PV-Erbb4^−/− mice showed significantly lower spontaneous firing rates in vivo (Figures 4H and 4I). Thus, the overall in vivo spontaneous activity of MCs appeared unchanged owing to opposing changes in excitatory and inhibitory subpopulations, and there was no true discrepancy between the ex vivo and in vivo results. We agree that in vivo recording of PV interneuron activity would be invaluable for understanding their functional state under physiological conditions. Unfortunately, this is technically unfeasible with the current experimental setup, primarily because of the sparse distribution of PV interneurons in the OB. As a complementary alternative, we characterised the key electrophysiological properties of PV interneurons in ex vivo slices (e.g. action potential and mEPSC, the revised Figure 7—figure supplement 1), which will provide additional insights into the underlying cellular mechanisms.

(6) Since PV neurons are required for gamma oscillations, why is it that KOs have higher gamma oscillations? Is it indeed the case that PV cells have a hypofunctional phenotype in this model? Again, recording from PV cells in vivo would help make sense of this.

Thank you for your valuable comments, which were critical for clarifying the functional consequences of ErbB4 knockout in PV interneurons. The elevated gamma oscillations in the OB of PV-Erbb4^-/- mice appear to be primarily driven by the increased action potential firing frequency of PV interneurons that we observed in OB slice recordings (the revised Figure 7—figure supplement 1). A similar phenomenon has been reported in the hippocampus (PMID:24050403).

Indeed, the PV cells displayed a hypofunctional phenotype in this model. Our optogenetic experiments provided direct evidence for this (the revised Figure 9—figure supplement 1). Specifically, optogenetic activation of PV interneurons in AAV-PV-Cre-injected mice (selective ErbB4 knockout in OB PV interneurons) induced weaker inhibitory postsynaptic currents (IPSCs) in MCs than in controls (the revised Figure 9—figure supplement 1). This indicates that ErbB4 loss induces PV interneurons to be more excitable, but impairs their ability to inhibit neighbouring MCs.

We acknowledge that in vivo recordings of PV interneurons would further clarify their functional state under physiological conditions. As noted earlier, this remains technically challenging using our current setup; however, our ex vivo mechanistic data and optogenetic findings collectively support these conclusions.

(7) A clearer picture of how PV cell inhibition changes with Erbb4 KO would be achieved with optogenetically evoked IPSPs, rather than changes in mini frequency.

Thank you for the comment. Based on your suggestions, we used optogenetics to activate PV interneurons and recorded the optogenetically evoked inhibitory postsynaptic currents (oIPSCs) in MCs. As shown in the revised Figure 9 and Supplementary Figure 1F and 1G, deleting ErbB4 in PV interneurons in the OB weakened the inhibitory modulation of MCs by PV interneurons.

Reviewer #3 (Public review):

Summary:

The authors investigate the role of ErbB4 in parvalbumin (PV) interneurons within the olfactory bulb (OB) and its regulation of odor discrimination behavior in mice. They demonstrate that odor discrimination increases ErbB4 kinase activity and that the loss of ErbB4 in the OB impairs the dishabituation of odor response and discrimination of complex odors. The study also characterizes the expression of ErbB4 in the OB, showing it is enriched in PV neurons. Furthermore, the authors utilize a mouse model in which ErbB4 is knocked out in PV neurons and perform a variety of behavioral, electrophysiological, and local field potential (LFP) recording experiments to characterize alterations in olfactory bulb activity. They then use a model in which ErbB4 is specifically knocked out in PV neurons in the OB and show that this manipulation disrupts odor-related behaviors in mice.

Strengths:

The study's strengths lie in its use of a diverse range of techniques, including RNAscope, IHC, and Western blotting, to assess the presence of ErbB4 in PV neurons within the OB. Additionally, the authors employ various behavioral tests to evaluate the effects of ErbB4 manipulation in different mouse models, alongside comprehensive electrophysiological experiments and LFP recordings to examine the impact of these manipulations on OB physiology.

Weaknesses:

While the data presented in this paper are interesting, several major concerns reduce my enthusiasm for this study, as outlined below:

(1) In reviewing Figure 1C/D, there are several concerns regarding the clarity and interpretation of the data:

(a) While the Western blot for ErbB4 in other figures (Figure 1F, 2I) of the manuscript shows a clear single band, the blot presented in Figure 1C (for both p-ErbB4 and total ErbB4) shows multiple bands, which is unexpected. This discrepancy raises concerns about the consistency of the results.

(b) The data presented in Figure 1D uses only 3 mice per group, and the reported p-value of 0.0492, while technically significant, is very close to the threshold. This raises concerns about the robustness of the finding, especially given the small sample size. Additionally, the p-ErbB4 band intensity in the Go/No-Go condition in Figure 1C does not appear to show a clear increase over the Go/Go condition, which is not congruent with the bar graph in Figure 1D showing a 50% increase in p-ErbB4/ErbB4 levels.

(c) It is a standard practice in many journals to include full, uncropped Western blot images as supplementary material. This transparency helps ensure that no bands are selectively shown or omitted and increases confidence in the presented data.

Thank you for your comment and thoughtful suggestion.

(a) The multiple bands observed for both p-ErbB4 and total ErbB4 in the original Figure 1C are likely attributable to the high concentration of the primary antibody used initially (Santa Cruz Biotechnology), which has since been discontinued. In the revised manuscript, we have replaced the original antibody with an anti-ErbB4 antibody (Cat# 4795, Cell Signalling Technology), which showed a single ErbB4 band (the revised Figure 1C). To detect p-ErbB4, we first performed immunoprecipitation with a phosphorylated tyrosine antibody to enrich the total phosphorylated proteins, followed by immunoblotting for ErbB4.

(b) According to your comments, we have expanded the sample size to four mice per group and modified the statistical test to an unpaired t-test in the revised Figure 1D.

(c) We included all relevant uncropped blot images in the Supplementary Material (the revised Figure 1, 2—figure supplement 1).

(2) In Figure 2, the authors used the anti-ErbB4 antibody sc-283 from Santa Cruz to assess the expression of ErbB4 in PV neurons and the absence of its expression in PV-ErbB4 knock-out mice. However, this particular antibody has been shown to produce non-specific bands in Western blotting and also generate non-specific labeling in IHC. This non-specificity has been demonstrated in Vullhorst et al. (2009, J Neurosci), raising significant concerns about the reliability of the data generated using this antibody.

Thank you for the comment. As you have indicated, the non-specificity of the anti-ErbB4 antibody sc-283 has been reported in J Neurosci (Vullhorst et al, 2009). These antibodies have been widely used in numerous recent studies (PMID:39543371 and PMID:41297670), indicating their utility for assessing ErbB4 expression under appropriate experimental conditions (primary antibody dilution and incubation conditions). As shown in the revised Figure 2I and 2J, the absence of ErbB4 expression in PV-ErbB4 knock-out mice proved the specificity of the antibody for immunofluorescence staining. To address these potential concerns, we conducted a rigorous validation tailored to our model. In the revised manuscript, we complemented the protein-level detection with RT-PCR, which directly validated the specific knockout of Erbb4 mRNA in PV neurones (the revised Figure 2F-H). Additionally, we performed follow-up immunofluorescence staining experiments using a well-validated anti-ErbB4 antibody (19943-1-AP, Proteintech; see PMID: 37060105) to assess the expression of ErbB4 in PV neurones (the revised Figure 9B and 9C).

(3) In reviewing the statistical analysis for the series of odor discrimination tests, there could be a potential issue with the clarity of the significance testing. Although the figure legend reports the F and p values from the two-way ANOVA, it is unclear whether these values represent the main effects or the results of a post hoc test. Additionally, it is not clear whether the asterisk in the figures reflects significance from a post hoc test or from the overall ANOVA. The methods section does not explicitly state whether a post hoc test was performed to assess differences between the knockout and control groups. Given that the tests were conducted across multiple days or conditions, a post hoc test that can adjust for multiple comparisons would be necessary to accurately identify where specific differences between the groups exist.

Thank you for your comment and suggestion. For the odour discrimination tests, two-way ANOVA was followed by Tukey’s post hoc adjustment for multiple pairwise comparisons, which is explicitly stated in the revised Methods section (Lines 832-833). According to your suggestions, we have revised the figure asterisks to indicate significant post hoc differences between the groups.

(4) Throughout the manuscript, the authors use different mouse models, including ErbB4 knockout specifically in the OB (AAV-Cre-GFP), ErbB4 knockout in PV interneurons throughout the brain (PV-ErbB4-/-), and ErbB4 knockout in PV interneurons within the OB (AAV-PV-Cre-GFP). For Figures 4 and 5, the authors use the PV-ErbB4-/- model to examine odor-evoked activity and neural oscillations within the OB. Since the knockout affects PV interneurons across the entire brain, it is difficult to disentangle whether the observed changes in the OB are due to local effects or broader network alterations elsewhere in the brain.

Thank you for the comment. We first clarify the rationale for initially using the whole-brain PV-Erbb4^-/- model: this model is well-validated and widely adopted in in vivo electrophysiological studies targeting brain region-specific phenomena, such as regulating synaptic plasticity in the hippocampus (PMID:24050403) and modulating sensory coding in the cortex (PMID: 37069344).

Additionally, PV interneurons in the OB are local-projection neurones that exert stronger and more extensive inhibitory effects on M/TCs, a key feature that restricts their functional impact primarily to the local OB circuit rather than broader cross-brain network interactions, further supporting the relevance of the global model for OB-focused research.

Furthermore, local AAV-Cre injections have notable experimental limitations in our electrophysiological recordings. Stereotaxic infusion induces mechanical trauma and local inflammation in the OB, altering basal circuit activity independent of ErbB4 deletion. AAV also yields incomplete mosaic gene ablation among PV interneurons, introducing a variable knockout efficiency that complicates the interpretation of local electrophysiological readouts. In comparison, the global PV-Erbb4^-/- line mediates uniform, complete ErbB4 deletion across all PV interneurons, avoiding viral artefacts and rendering our OB electrophysiological measurements more reliable for assessing endogenous local circuit function.

(5) While the electrophysiological experiments shown in Figures 6-8 provide valuable insights into the reduced inhibition to MCs in PV-ErbB4 knockout mice, it appears that the authors did not record from PV interneurons themselves. Since PV interneurons are central to the proposed mechanism, directly recording them would provide critical information on how the ErbB4 knockout affects their intrinsic properties, synaptic inputs, and firing behavior. Without these direct recordings, the conclusions about the specific role of PV neurons in regulating MC activity remain somewhat indirect. Prior studies have established that knockout of ErbB4 in PV interneurons reduces mEPSC frequency in PV neurons (Del Pino et al., 2013).

Thank you for your valuable comment and suggestion. According to your suggestions, we have supplemented the electrophysiological experiments (the revised Figure 7—figure supplement 1) with direct recordings from PV interneurons in ex vivo slices. These recordings revealed that ErbB4 knockout alters some properties of PV interneurons (e.g. action potential frequency), reduces mEPSC frequency (consistent with Del Pino et al., 2013), and modulates their firing behaviour, directly confirming that ErbB4 deletion affects PV interneurons.

(6) In Figure 9, the authors knock out ErbB4 in PV neurons in the OB with AAV-PV-Cre-GFP and show with western blotting that ErbB4 expression is reduced in the mouse injected with AAV-PV-Cre-GFP. However, it is not clear whether ErbB4 was selectively knocked out in PV neurons without the quantification from IHC assays.

Thank you for the comment. To verify the selective knockout of ErbB4 in OB PV neurones, we performed an additional experiment: immunofluorescence co-staining for PV and ErbB4; quantitative analysis confirmed a significant reduction of ErbB4 in PV interneurons in AAV-PV-Cre–injected mice (the revised Figure 9B and 9C).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Other concerns:

(1) No supplemental Figure 1 was shown.

We apologise for the oversight. Supplemental Figure have been included in the revised manuscript (the revised Figure 2—figure supplemental 2).

(2) In line 59, page 3, abbreviations of mitral/tufted cells (M/TCs) or "MCs" were confusing.

We have clarified the abbreviation by explicitly defining "mitral cells (MCs)", with "M/TCs" retained for mitral/tufted cells to avoid ambiguity (Line 56-59).

(3) The quality of blots in Figure 1C was less satisfactory, with lots of noisy bands. Maybe antibodies from Cell Signaling should be used.

We optimised the experiment as suggested. In the revised Figure 1C, we have used an anti-ErbB4 antibody (Cat# 4795, Cell Signalling Technology) combined with the immunoprecipitation-immunoblotting workflow.

(4) The authors should describe the serotype as well as the promoters of AAV-Cre-GFP used in the experiments.

As you suggested, we have supplemented the details of AAV-Cre-GFP in the Methods section: Viruses driven by the CAG promoter, including pAOV-CAG-EGFP-T2A-Cre (catalogue No. CN396, serotype AAV2/8) and pAOV-CAG-EGFP-2A (catalogue No. CN394, serotype AAV2/8) were purchased from Obio Technology, Shanghai, China (Lines 568-571).

(5) The authors should describe the binary mixtures of isoamyl acetate Vs. Heptanone. Simply 6/4 Vs. 4/6 is not easy to follow.

As you suggested, we have clarified the binary odour mixtures in the Results section: (60%/40% binary mixtures of these odours, "6/4" refers to 60% isoamyl acetate + 40% heptanone, and "4/6" refers to 40% isoamyl acetate + 60% heptanone, in volume) (Lines 111-113).

(6) Figure 1G, "0 limonene" AAV-Cre-GFP group did not show the error bar.

We apologise for the omission—error bars for the "0 limonene" AAV-Cre-GFP group have been added to the revised Figure 1.

(7) Figure 2A, the green signal for ErbB4 was not that strong, it was hard to visualize the expression of ErbB4 in five layers of OB.

Thank you for the comment. The revised Figure 2A shows an enhanced green signal for ErbB4, clearly indicating its distribution in all OB layers.

(8) The authors should clearly label or indicate the cell type of neurons recorded in Figure 6, Figure 7, and Figure 8A-8C.

As you suggested, we have clearly labelled the cell types in the revised Figures 6, 7, and 8A–8C: all recorded neurones are mitral cells (MCs).

(9) line 320-321, page 14, "Figures 8F and 8G, a burst of conditioning 320 stimuli (40 pulses at 100 Hz)", the authors should indicate the stimuli as a tick or scale on Figures 8F and 8I.

As per your suggestion, we have added scales and vertical ticks to the revised Figures 8F and 8I to indicate the timing of the conditioning stimuli (40 pulses at 100 Hz).

Reviewer #2 (Recommendations for the authors):

(1) Figure 1F is not quantified.

As suggested, we have supplemented the quantitative analyses of Figure 1F (see the revised Figure 1G) and the statistical details in the revised legend.

(2) Figures 2G and H are not quantified.

As suggested, we have supplemented the quantitative analyses of Figures 2G and 2H (see the revised Figures 2H and 2J), and statistical details are provided in the revised figure legends.

(3) Bar plots with standard error are not suitable for visualizing the distribution of data. Either show violin plots, histograms, or raw data points throughout.

As suggested, we included the raw data points in the revised manuscript.

(4) Figure 3 legend - (Wen et al., 2010) citations repeated.

Thank you for the comment. We have removed the repeated (Wen et al., 2010) citation in the revised manuscript.

(5) Does Ebbr4 deletion change the waveform shape of PV+ cells? This could influence spike sorting and cell classification.

Thank you for the comment. According to your recommendations, we performed additional ex vivo patch-clamp recordings of PV+ interneurons, which showed that ErbB4 knockout did not alter their action potential waveform shape (e.g. spike amplitude and half-width, the revised Figure 7—figures supplement 1D and 1E). Importantly, this knockout also did not directly affect the spike waveform shapes of M/TCs in vivo (e.g. peak-to-valley ratio and half-valley width, the revised Figure 4—figures supplement 1C-1E). Therefore, we speculate that spike sorting and cell classification were not affected.

(6) Line 327 - is this really a measure of inhibitory circuit plasticity?

Thank you for the comment. We have replaced "inhibitory circuit plasticity" with "inhibitory circuit activity" and comprehensively updated all relevant instances throughout the manuscript to ensure consistent use of the term.

(7) In the discussion: "Another interesting finding is that the changes in spontaneous firing rate differed for odor-evoked excitatory and inhibitory responses in vivo, suggesting that ErbB4 in PV interneurons dynamically regulates the spontaneous activity of M/TCs in response to different odors." The significance of this finding is not discussed and it is not clear what this result means. For example, does this relate to a "winner-take-all scenario"?

Thank you for the comment. According to your recommendations, we have discussed the significance of this finding in the revised Discussion section (Lines 438-449):

This result reveals a dual regulatory role of ErbB4 in PV interneurons in olfactory coding. For odour-evoked excitatory responses, PV interneurons (via ErbB4) constrain M/TC spontaneous firing at a low baseline, minimising background noise and enhancing the SNR. In contrast, the inhibitory responses maintain a higher spontaneous firing baseline to accentuate odour-evoked suppression. This regulation amplifies the "excitation of excited M/TCs and inhibition of inhibited M/TCs," a hallmark of the OB’s "winner-take-all" mechanism that sharpens odour identity coding, which is critical for odour discrimination. These data confirm that ErbB4 in PV interneurons does not exert a global modulation, but dynamically tailors M/TC spontaneous activity to odour-evoked responses, thereby optimising the ability of the OB to resolve olfactory cues.

(8) The discussion on linking AD with odor discrimination impairments, and the potential role of Erbb4 was interesting. However the discussion of "fluctuation status" is not defined. What does this refer to?

According to the comment, we have added the following wording to the Discussion section (Lines 478-497):

As referenced by Iemi et al. (2022), "fluctuation status" herein refers to the spontaneous, endogenous fluctuations in neural activity that occur in the brain prior to sensory stimulation (i.e. pre-stimulus) or in the absence of external sensory input. External cues do not drive this state but arise from intrinsic neural dynamics, and it is primarily characterised by changes in the power of neural oscillations across multiple frequency bands (e.g., alpha, beta, and their neighbouring frequencies, collectively termed "alpha+ band" in Iemi et al. (2022)). Critically, this fluctuation status is distinct from stimulus-evoked neural responses; it reflects a pre-existing "baseline" state of the neural system that modulates subsequent sensory processing and behaviour. Consistent with Iemi et al. (2022), previous work has established that such ongoing neural fluctuations strongly predict behavioural variability in both health (e.g. slower reaction times and reduced perceptual accuracy) and disease (e.g. age-related cognitive decline and schizophrenia) by regulating neuronal excitability. In our study, we extended this concept to olfactory function, focusing on "broad ongoing fluctuations" (encompassing multiple frequency bands) and linking their dynamics to OB output. Specifically, these fluctuations influence the ability of the OB to support rapid recovery from olfactory adaptation and to mediate complex odour discrimination, thereby uncovering a novel role for endogenous neural fluctuation status in olfactory circuit function.

Reviewer #3 (Recommendations for the authors):

(1) For Figure 1C, I strongly recommend that the authors include full, uncropped Western blot images for both p-ErbB4 and total ErbB4 as supplementary material to improve the transparency and credibility of the findings.

As you suggested, we have supplemented the full, uncropped western blot images for both phosphorylated ErbB4 (p-ErbB4) and total ErbB4, as the revised Figures 1 and 2 and Supplementary Figure 1.

(2) The authors should either validate the specificity of the sc-283 antibody in their experimental conditions or consider using a more specific antibody for ErbB4 to ensure the reliability of their data.

Thank you for your comments. As shown in the revised Figure 2I and 2J, the absence of ErbB4 expression in PV-ErbB4 knock-out mice proved the specificity of the antibody for immunofluorescence staining. To address these potential concerns, we conducted a rigorous validation tailored to our model. In the revised manuscript, we complemented the protein-level detection with RT-PCR, which directly validated the specific knockout of Erbb4 mRNA in PV neurones (the revised Figure 2F-H). Additionally, we performed follow-up immunofluorescence staining experiments using a well-validated anti-ErbB4 antibody (19943-1-AP, Proteintech; see PMID: 37060105) to assess the expression of ErbB4 in PV neurones (the revised Figure 9B and 9C).

(3) I recommend that the authors clarify in the methods section whether a post hoc test with multiple comparison adjustments (e.g., Tukey's HSD or Bonferroni) was conducted for the behavioral tests presented throughout the study. If no such test was performed, it would be beneficial to include one to ensure accurate identification of significant differences between groups across the different experimental days or conditions.

For the behavioural tests, we confirmed that two-way ANOVA was followed by Tukey’s post hoc adjustment for multiple pairwise comparisons, which has been clarified in the revised Methods section (Lines 832-833). Additionally, we have revised the asterisks in the relevant figures to clearly indicate significant post-hoc differences between the groups.

(4) The rationale for using a whole-brain PV-specific knockout model (PV-ErbB4-/-) to assess OB-specific phenomena in Figures 4 and 5 should be clarified. I also recommend the authors provide or conduct additional experiments with OB-specific knockouts to determine whether the effects observed in Figures 4 and 5 are directly attributable to the loss of ErbB4 in PV interneurons within the OB.

To clarify the rationale, the whole-brain PV-Erbb4^−/− mouse line was initially used to characterise the overall functional relevance of ErbB4 in PV interneurons for OB activity and odour-evoked responses. We clarified this rationale in the revised Results section (Lines 210-211 and Lines 250-251).

As elaborated above, AAV-mediated OB-specific knockouts suffer from injection-induced tissue injury, incomplete mosaic recombination, and uncertainties in local electrophysiological recordings, which would compromise data reliability. Moreover, OB PV interneurons act predominantly as local circuit neurones; therefore, the phenotypes observed in Figures 4 and 5 most plausibly arise from intrinsic ErbB4 deletion within bulbar PV cells rather than from long-range brain-wide network changes. For these reasons, we consider our current global PV-Erbb4^−/− model appropriate to interpret the local OB circuit effects here, and we outline OB-targeted knockout manipulations as a direction for future independent follow-up research.

(5) To strengthen their conclusions drawn from Figures 6-8, the authors should perform direct recordings from PV interneurons in the OB to assess how the ErbB4 knockout affects their intrinsic properties, synaptic inputs, and firing behavior. This would provide more direct evidence of PV interneuron dysfunction in the knockout mice.

According to your recommendations, we have performed direct recordings of OB PV interneurons using ex vivo patch-clamp electrophysiology (the revised Figure 7—figures supplementary 1). These recordings reveal that ErbB4 knockout affects the intrinsic properties of PV interneurons, synaptic inputs (reduced mEPSC frequency and amplitude, the revised Figure 7—figures supplementary 1A and 1B), and firing behaviour (increased action potential frequency, the revised Figure 7—figures supplementary 1C), directly confirming that ErbB4 deletion affects PV interneurons themselves. These results provide direct evidence of PV interneuron dysfunction in the knockout mice.

(6) I recommend that the authors assess molecular markers of PV interneuron inhibition, such as GAD67, in PVIs. This would help link the ErbB4 knockout to impaired PV interneuron function and its downstream effects on MC inhibition.

Thank you for the comment. We attempted to detect GAD67 in OB PVIs using multiple commercial antibodies but encountered consistent technical limitations (e.g. weak signal specificity and high background) that precluded reliable quantitative analysis.

To address this gap, we used optogenetics to activate PV interneurons and recorded optogenetically evoked inhibitory postsynaptic currents (oIPSCs) in MCs. As shown in the revised Figure 9 and Supplementary Figure 1F and 1G, deleting ErbB4 of PV interneurons in the OB weakened the inhibitory modulation of MCs by PV interneurons. This result provides direct electrophysiological evidence linking ErbB4 knockout to impaired PV interneuronal function and its downstream effects on MC inhibition.

(7) For Figure 9, I recommend that the authors perform IHC to show that ErbB4 is selectively knocked out in PV neurons but not in non-PV neurons within the OB, as the Western blot analysis alone does not provide this specificity.

According to your recommendations, we performed an additional key experiment: immunofluorescence co-staining for PV and ErbB4, with quantitative analysis confirming a significant reduction in ErbB4 in OB PV interneurons, but not in non-PV cells, in AAV-PV-Cre–injected mice (the revised Figure 9B and 9C).