Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Englert et al. proposed a functional connectome-based Hopfield artificial neural network (fcHNN) architecture to reveal attractor states and activity flows across various conditions, including resting state, task-evoked, and pathological conditions. The fcHNN can reconstruct characteristics of resting-state and task-evoked brain activities. Additionally, the fcHNN demonstrates differences in attractor states between individuals with autism and typically developing individuals.

Strengths:

(1) The study used seven datasets, which somewhat ensures robust replication and validation of generalization across various conditions.

(2) The proposed fcHNN improves upon existing activity flow models by mimicking artificial neural networks, thereby enhancing the representational ability of the model. This advancement enables the model to more accurately reconstruct the dynamic characteristics of brain activity.

(3) The fcHNN projection offers an interesting visualization, allowing researchers to observe attractor states and activity flow patterns directly.

We are grateful to the reviewer for highlighting the robustness of our findings across multiple datasets and for appreciating the novelty and representational advantages of our fcHNN model (which has been renamed to fcANN in the revised manuscript).

Weaknesses:

(1) The fcHNN projection can offer low-dimensional dynamic visualizations, but its interpretability is limited, making it difficult to make strong claims based on these projections. The interpretability should be enhanced in the results and discussion.

We thank the reviewer for these important points. We agree that the interpretability of the low-dimensional projection is limited. In the revised manuscript, we have reframed the fcANN projection primarily as a visualization tool (see e.g. line 359) and moved the corresponding part of Figure 2 to the Supplementary Material (Supplementary Figure 2). We have also implemented a substantial revision of the manuscript, which now directly links our analysis to the novel theoretical framework of self-orthogonalizing attractor networks (Spisak & Friston, 2025), opening several new avenues in terms of interpretation and shedding light on the computational principles underlying attractor dynamics in the brain (see the revised introduction and the new section “Theoretical background”, starting at lines 128, but also the Mathematical Appendices 1-2 in the Supplementary Material for a comprehensive formal derivation). As part of these efforts, we now provide evidence for the brain’s functional organization approximating a special, computationally efficient class of attractor networks, the so-called Kanter-Sompolinsky projector network (Figure 2A-C, line 346, see also our answer to your next comment). This is exactly, what the theoretical framework of free-energy-minimizing attractor networks predicts.

(2) The presentation of results is not clear enough, including figures, wording, and statistical analysis, which contributes to the overall difficulty in understanding the manuscript. This lack of clarity in presenting key findings can obscure the insights that the study aims to convey, making it challenging for readers to fully grasp the implications and significance of the research.

We have thoroughly revised the manuscript for clarity in wording, figures (see e.g. lines 257, 482, 529 in the Results and lines 1128, 1266, 1300, 1367 in the Methods). We carefully improved statistical reporting and ensured that we always report test statistics, effect sizes and clearly refer to the null modelling approach used (e.g. lines 461, 542, 550, 565, 573, 619, as well as Figures 2-4). As absolute effect sizes, in many analyses, do not have a straightforward interpretation, we provided Glass’ , as a standardized effect size measure, expressing the distance of the true observation from the null distribution as a ratio of the null standard deviation. To further improve clarity, we now clearly define our research questions and the corresponding analyses and null models in the revised manuscript, both in the main text and in two new tables (Tables 1 and 2). We denoted research questions and null model with Q1-7 and NM1-5, respectively and refer to them at multiple instances when detailing the analyses and the results.

Reviewer #2 (Public Review):

Summary:

Englert et al. use a novel modelling approach called functional connectome-based Hopfield Neural Networks (fcHNN) to describe spontaneous and task-evoked brain activity and the alterations in brain disorders. Given its novelty, the authors first validate the model parameters (the temperature and noise) with empirical resting-state function data and against null models. Through the optimisation of the temperature parameter, they first show that the optimal number of attractor states is four before fixing the optimal noise that best reflects the empirical data, through stochastic relaxation. Then, they demonstrate how these fcHNN-generated dynamics predict task-based functional activity relating to pain and self-regulation. To do so, they characterise the different brain states (here as different conditions of the experimental pain paradigm) in terms of the distribution of the data on the fcHNN projections and flow analysis. Lastly, a similar analysis was performed on a population with autism condition. Through Hopfield modeling, this work proposes a comprehensive framework that links various types of functional activity under a unified interpretation with high predictive validity.

Strengths:

The phenomenological nature of the Hopfield model and its validation across multiple datasets presents a comprehensive and intuitive framework for the analysis of functional activity. The results presented in this work further motivate the study of phenomenological models as an adequate mechanistic characterisation of large-scale brain activity.

Following up on Cole et al. 2016, the authors put forward a hypothesis that many of the changes to the brain activity, here, in terms of task-evoked and clinical data, can be inferred from the resting-state brain data alone. This brings together neatly the idea of different facets of brain activity emerging from a common space of functional (ghost) attractors.

The use of the null models motivates the benefit of non-linear dynamics in the context of phenomenological models when assessing the similarity to the real empirical data.

We thank the reviewer for recognizing the comprehensive and intuitive nature of our framework and for acknowledging the strength of our hypothesis that diverse brain activity facets emerge from a common resting state attractor landscape.

Weaknesses:

While the use of the Hopfield model is neat and very well presented, it still begs the question of why to use the functional connectome (as derived by activity flow analysis from Cole et al. 2016). Deriving the functional connectome on the resting-state data that are then used for the analysis reads as circular.

We agree that starting from functional couplings to study dynamics is in stark contrast with the common practice of estimating the interregional couplings based on structural connectome data. We now explicitly discuss how this affects the scope of the questions we can address with the approach, with explicit notes on the inability of this approach to study the structure-function coupling and its limitations in deriving mechanistic insights at the level of biophysical implementation.

Line 894:

“The proposed approach is not without limitations. First, as the proposed approach does not incorporate information about anatomical connectivity and does not explitly model biophysical details. Thus, in its present form, the model is not suitable to study the structure-function coupling and cannot yiled mechanistic explanations underlying (altered) polysynaptic connections, at the level of biophysical details.”

We are confident, however, that our approach is not circular. At the high level, our approach can be considered as a function-to-function generative model, with twofold aims.

First, we link large-scale brain dynamics to theoretical artificial neural network models and show that the functional connectome display characteristics that render it as an exceptionally “well-behaving” attractor network (e.g. superior convergence properties, as contrasted against appropriate respective null models). In the revised manuscript, we have significantly improved upon this aspect by explicitly linking the fcANN model to the theoretical framework of self-orthogonalizing attractor networks (Spisak & Friston, 2025) (see the revised introduction and the new section “Theoretical background”, starting at lines 128, but also the Mathematical Appendices 1-2 in the Supplementary Material for a comprehensive formal derivation). As part of these efforts, we now provide evidence for the brain’s functional organization approximating a special, computationally efficient class of attractor networks, the so-called Kanter-Sompolinsky projector network (Figure 2A-C, line 346, see also our answer to your next comment). This is exactly, what the theoretical framework of free-energy-minimizing attractor networks predicts. This result is not circular, as the empirical model does not use the key mechanism (the Hebbian/anti-Hebbian learning rule) that induces self-orthogonalization in the theoretical framework. We clarify this in the revised manuscript, e.g. in line 736.

Second, we benchmark ability of the proposed function-to-function generative model to predict unseen data (new datasets) or data characteristics that are not directly encompassed in the connectivity matrix (e.g. non-Gaussian conditional dependencies, temporal autocorrelation, dynamical responses to perturbations on the system). These benchmarks are constructed against well defined null models, which provide reasonable references. We have now significantly improved the discussion of these null models in the revised manuscript (Tables 1 and 2, lines 257). We not only show, that our model - when reconstructing resting state dynamics - can generalize to unseen data over and beyond what is possible with the baseline descriptive measure (e.g. covariance measures and PCA), but also demonstrate the ability of the framework to reconstruct the effects of perturbations on this dynamics (such as task-evoked changes), based solely on the resting state data form another sample.

If the fcHNN derives the basins of four attractors that reflect the first two principal components of functional connectivity, it perhaps suffices to use the empirically derived components alone and project the task and clinical data on it without the need for the fcHNN framework.

We are thankful for the reviewer for highlighting this important point, which encouraged us to develop a detailed understanding of the origins of the close alignment between attractors and principal components (eigenvectors of the coupling matrix) and the corresponding (approximate) orthogonality. Here, we would like to emphasize that the attractor-eigenvector correspondence is by no means a general feature of any arbitrary attractor network. In fact, such networks are a very special class of attractor neural networks (the so-called Kanter-Sompolinsky projector neural network (Kanter & Sompolinsky, 1987)), with a high degree of computational efficiency, maximal memory capacity and perfect memory recall. It has been rigorously shown that in such networks, the eigenvectors of the coupling matrix (i.e. PCA on the timeseries data) and the attractors become equivalent (Kanter & Sompolinsky, 1987). This in turn made us ask the question, what are the learning and plasticity rules that drive attractor networks towards developing approximately orthogonal attractors? We found that this is a general tendency of networks obeying the free energy principle ( Figure 2A-C, line 346, see also our answer to your next comment). The formal derivation of this framework in now presented in an accompanying theoretical piece (Spisak & Friston, 2025). In the revised manuscript, we provide a short, high-level overview of these results (in the Introduction form line 55 and in the new section “Theoretical background”, line 128, but also the Mathematical Appendices 1-2 in the Supplementary Material for a comprehensive formal derivation). According to this new theoretical model, attractor states can be understood as a set of priors (in the Bayesian sense) that together constitute an optimal orthogonal basis, equipping the update process (which is akin to a Markov-chain Monte Carlo sampling) to find posteriors that generalize effectively within the spanned subspace. Thus, in sum, understanding brain function in terms of attractor dynamics - instead of PCA-like descriptive projections - provides important links towards a Bayesian interpretation of brain activity. At the same time, the eigenvector-attractor correspondence also explains, why descriptive decomposition approaches, like PCA or ICA are so effective at capturing the dynamics of the system, at the first place.

As presented here, the Hopfield model is excellent in its simplicity and power, and it seems suited to tackle the structure-function relationship with the power of going further to explain task-evoked and clinical data. The work could be strengthened if that was taken into consideration. As such the model would not suffer from circularity problems and it would be possible to claim its mechanistic properties. Furthermore, as mentioned above, in the current setup, the connectivity matrix is based on statistical properties of functional activity amongst regions, and as such it is difficult to talk about a certain mechanism. This contention has for example been addressed in the Cole et al. 2016 paper with the use of a biophysical model linking structure and function, thus strengthening the mechanistic claim of the work.

We agree that investigating how the structural connectome constraints macro-scale dynamics is a crucial next step. Linking our results with the theoretical framework of self-orthogonalizing attractor networks provides a principled approach to this, as the “self-orthogonalizing” learning rule in the accompanying theoretical work provides the opportunity to fit attractor networks with structural constraints to functional data, shedding light on the plastic processes which maintain the observed approximate orthogonality even in the presence of these structural constraints. We have revised the manuscript to clarify that our phenomenological approach is inherently limited in its ability to answer mechanistic questions at the level of biophysical details (lines 894) and discuss this promising direction as follows:

Lines 803:

“A promising application of this is to consider structural brain connectivity (as measured by diffusion MRI) as a sparsity constraint for the coupling weights and then train the fcANN model to match the observed resting-state brain dynamics. If the resulting structural-functional ANN model is able to closely match the observed functional brain substate dynamics, it can be used as a novel approach to quantify and understand the structural functional coupling in the brain”.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The statistical analyses are poorly described throughout the manuscript. The authors should provide more details on the statistical methods used for each comparison, as well as the corresponding statistics and degrees of freedom, rather than solely reporting p-values.

We thank the reviewer for pointing this out. We have revised the manuscript to include the specific test statistics, precise p-values and raw effect sizes for all reported analyses to ensure full transparency and replicability, see e.g. lines 461, 542, 550, 565, 573, 619, as well as Figures 2-4. Additionally, as absolute effect sizes - in many analyses - do not have a straightforward interpretation, we provided Glass’ Δ, as a standardized effect size measure, expressing the distance of the true observation from the null distribution as a ratio of the null standard deviation.

We have also improved the description of the statistical methods used in the manuscript (lines 1270, 1306, 1339, 1367, 1404) and added two overview tables (Tables 1 and 2) that summarize the methodological approaches and the corresponding null models.

Furthermore, we have fully revised the analysis corresponding to noise optimization. We only retained null model 2 (covariance-matched Gaussian) in the main text and on Figure 3, and moved model 1 (spatial phase randomization) into the Supplementary Material (Supplementary Figure 6) and is less appropriate for this analysis (trivially significant in all cases). Furthermore, as test statistic, no we use a Wasserstein distance between the 122-dimensional empirical and the simulated data (instead of focusing on the 2-dimensional projection). This analysis now directly quantifies the capacity of the fcANN model to capture non-Gaussian conditionals in the data.

(2) The convergence procedure is not clearly explained in the manuscript. Is this an optimization procedure to minimize energy? If so, the authors should provide more details about the optimizer used.

We apologize for the lack of clarity. The convergence is not an optimization procedure per se, in a sense that it does not involve any external optimizer. It is simply the repeated (deterministic) application of the same update rule also known from Hopfield networks or Boltzmann machines. However, as detailed in the accompanying theoretical paper, this update rule (or inference rule) inherently solves and optimization problem: it performs gradient descent on the free energy landscape of the network. As such, it is guaranteed to converge to a local free energy minimum in the deterministic case. We have clarified this process in the Results and Methods sections as follows:

Line 161:

“Inference arises from minimizing free energy with respect to the states \sigma. For a single unit, this yields a local update rule homologous to the relaxation dynamics in Hopfield networks”.

Line 181:

“In the basis framework (Spisak & Friston, 2025), inference is a gradient descent on the variational free energy landscape with respect to the states σ and can be interpreted as a form of approximate Bayesian inference, where the expected value of the state σ_i is interpreted as the posterior mean given the attractor states currently encoded in the network (serving as a macro-scale prior) and the previous state, including external inputs (serving as likelihood in the Bayesian sense)”.

Line 1252:

“As the inference rule was derived as a gradient descent on free energy, iterations monotonically decrease the free energy function and therefore converge to a local free‑energy minimum without any external optimizer. Thus, convergence does not require any optimization procedure with an external optimizer. Instead, it arises as the fixed point of repeated local inference updates, which implement gradient descent on free energy in the deterministic symmetric case.”

(3) In Figure 2G, the beta values range from 0.035 to 0.06, but they are reported as 0.4 in the main text and the Supplementary Figure. Please clarify this discrepancy.

We are grateful to the reviewer for spotting this typo. The correct value for β is 0.04, as reported in the Methods section. We have corrected this inconsistency in the revised manuscript and as well as in Supplementary Figure 5.

(4) Line 174: What type of null model was used to evaluate the impact of the beta values? The authors did not provide details on this anywhere in the manuscript.

We apologize for this omission. The null model is based on permuting the connectome weights while retaining the matrix symmetry, which destroys the specific topological structure but preserves the overall weight distribution. We have now clarified this at multiple places in the revised manuscript (lines 432, Table 1-2, Figure 2), and added new overview tables (Tables 1 and 2) to summarize the methodological approaches and the corresponding null models.

(5) Figure 3B: It appears that the authors only demonstrate the reproducibility of the “internal” attractor across different datasets. What about other states?

Thank you for noticing this. We now visualize all attractor states in Figure 3B (note that these essentially consist of two symmetric pairs).

(6) Figure 3: What does “empirical” represent in Figure 3? Is it PCA? If the “empirical” method, which is a much simpler method, can achieve results similar to those of the fcHNN in terms of state occupancy, distribution, and activity flow, what are the benefits of the proposed method? Furthermore, the authors claim that the explanatory power of the fcHNN is higher than that of the empirical model and shows significant differences. However, from my perspective, this difference is not substantial (37.0% vs. 39.9%). What does this signify, particularly in comparison to PCA?

This is a crucial point that is now a central theme of our revised manuscript. The reviewer is correct that the “empirical” method is PCA. PCA - by identifying variance-heavy orthogonal directions - aims to explain the highest amount of variance possible in the data (with the assumption of Gaussian conditionals). While empirical attractors are closely aligned to the PCs (i.e. eigenvectors of the inverse covariance matrix, as shown in the new analysis Q1), the alignment is only approximate. We basically take advantage of this small “gap” to quantify, weather attractor states are a better fit to the unseen data than the PCs. Obviously, due to the otherwise strong PC-attractor correspondence, this is expected to be only a small improvement. However, it is an important piece of evidence for the validity of our framework, as it shows that attractors are not just a complementary, perhaps “noisier” variety of the PCs, but a “substrate” that generalizes better to unseen data than the PCs themselves. We have revised the manuscript to clarify this point (lines 528).

Reviewer #2 (Recommendations For The Authors):

For clarity, it might be useful to define and use consistently certain key terms. Connectome often refers to structural (anatomical) connectivity unless defined specifically this should be considered, in Figure 1B title for example Brain state often refers to different conditions ie autism, neurotypical, sleep, etc... see for review Kringelbach et al. 2020, Cell Reports. When referring to attractors of brain activity they might be called substates.

We thank the reviewer for these helpful suggestions. We have carefully revised the manuscript to ensure our terminology is precise and consistent. We now explicitly refer to the “functional connectome” (including the title) and avoid using the too general term “brain state” and use “substates” instead.

In Figure 2 some terms are not defined. Noise is sigma in the text but elpsilon in the figure. Only in methods, the link becomes clear. Perhaps define epsilon in the caption for clarity. The same applies to μ in the methods. It is only described above in the methods, I suggest repeating the epsilon definition for clarity

We appreciate this feedback and apologize for the inconsistency. We have revised all figures and the Methods section to ensure that all mathematical symbols (including ε, σ, and μ) are clearly and consistently defined upon their first appearance and in all figure captions. For instance, noise level is now consistently referred to as ϵ. We improved the consistency and clarity for other terms, too, including:

functional connectome-based Hopfiled network (fcHNN) => functional connectivity-based attractor network (fcANN);

temperature => inverse temperature;

And improved grammar and language throughout the manuscript.

References

Kanter, I., & Sompolinsky, H. (1987). Associative recall of memory without errors. Physical Review A, 35(1), 380–392. 10.1103/physreva.35.380

Spisak T & Friston K (2025). Self-orthogonalizing attractor neural networks emerging from the free energy principle. arXiv preprint arXiv:2505.22749.

Author response:

The following is the authors’ response to the original reviews

We again thank the reviewers for their comments and recommendations. In response to the reviewer’s suggestions, we have performed several additional experiments, added additional discussion, and updated our conclusions to reflect the additional work. Specifically, we have performed additional analyses in female WT and Marco-deficient animals, demonstrating that the Marco-associated phonotypes observed in male mice (reduced adrenal weight, increased lung Ace mRNA and protein expression, unchanged expression of adrenal corticosteroid biosynthetic enzymes) are not present in female mice. We also report new data on the physiological consequences of increased aldosterone levels observed in male mice, namely plasma sodium and potassium titres, and blood pressure alterations in WT vs Marco-deficient male mice. In an attempt to address the reviewer’s comments relating to our proposed mechanism on the regulation of lung Ace expression, we additionally performed a co-culture experiment using an alveolar macrophage cell line and an endothelial cell line. In light of the additional evidence presented herein, we have updated our conclusions from this study and changed the title of our work to acknowledge that the mechanism underlying the reported phenotype remains incompletely understood. Specific responses to reviewers can be seen below.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The investigators sought to determine whether Marco regulates the levels of aldosterone by limiting uptake of its parent molecule cholesterol in the adrenal gland. Instead, they identify an unexpected role for Marco on alveolar macrophages in lowering the levels of angiotensin-converting enzyme in the lung. This suggests an unexpected role of alveolar macrophages and lung ACE in the production of aldosterone.

Strengths:

The investigators suggest an unexpected role for ACE in the lung in the regulation of systemic aldosterone levels.

The investigators suggest important sex-related differences in the regulation of aldosterone by alveolar macrophages and ACE in the lung.

Studies to exclude a role for Marco in the adrenal gland are strong, suggesting an extra-adrenal source for the excess Marco observed in male Marco knockout mice.

Weaknesses:

While the investigators have identified important sex differences in the regulation of extrapulmonary ACE in the regulation of aldosterone levels, the mechanisms underlying these differences are not explored.

The physiologic impact of the increased aldosterone levels observed in Marco -/- male mice on blood pressure or response to injury is not clear.

The intracellular signaling mechanism linking lung macrophage levels with the expression of ACE in the lung is not supported by direct evidence.

Reviewer #2 (Public Review):

Summary:

Tissue-resident macrophages are more and more thought to exert key homeostatic functions and contribute to physiological responses. In the report of O'Brien and Colleagues, the idea that the macrophage-expressed scavenger receptor MARCO could regulate adrenal corticosteroid output at steady-state was explored. The authors found that male MARCO-deficient mice exhibited higher plasma aldosterone levels and higher lung ACE expression as compared to wild-type mice, while the availability of cholesterol and the machinery required to produce aldosterone in the adrenal gland were not affected by MARCO deficiency. The authors take these data to conclude that MARCO in alveolar macrophages can negatively regulate ACE expression and aldosterone production at steady-state and that MARCO-deficient mice suffer from secondary hyperaldosteronism.

Strengths:

If properly demonstrated and validated, the fact that tissue-resident macrophages can exert physiological functions and influence endocrine systems would be highly significant and could be amenable to novel therapies.

Weaknesses:

The data provided by the authors currently do not support the major claim of the authors that alveolar macrophages, via MARCO, are involved in the regulation of a hormonal output in vivo at steady-state. At this point, there are two interesting but descriptive observations in male, but not female, MARCO-deficient animals, and overall, the study lacks key controls and validation experiments, as detailed below.

Major weaknesses:

(1) According to the reviewer's own experience, the comparison between C57BL/6J wild-type mice and knock-out mice for which precise information about the genetic background and the history of breedings and crossings is lacking, can lead to misinterpretations of the results obtained. Hence, MARCO-deficient mice should be compared with true littermate controls.

(2) The use of mice globally deficient for MARCO combined with the fact that alveolar macrophages produce high levels of MARCO is not sufficient to prove that the phenotype observed is linked to alveolar macrophage-expressed MARCO (see below for suggestions of experiments).

(3) If the hypothesis of the authors is correct, then additional read-outs could be performed to reinforce their claims: levels of Angiotensin I would be lower in MARCO-deficient mice, levels of Antiotensin II would be higher in MARCO-deficient mice, Arterial blood pressure would be higher in MARCO-deficient mice, natremia would be higher in MARCO-deficient mice, while kaliemia would be lower in MARCO-deficient mice. In addition, co-culture experiments between MARCO-sufficient or deficient alveolar macrophages and lung endothelial cells, combined with the assessment of ACE expression, would allow the authors to evaluate whether the AM-expressed MARCO can directly regulate ACE expression.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Corticosterone levels in male Marco -/- mice are not significantly different, but there is (by eye) substantially more variability in the knockout compared to the wild type. A power analysis should be performed to determine the number of mice needed to detect a similar % difference in corticosterone to the difference observed in aldosterone between male Marco knockout and wild-type mice. If necessary the experiments should be repeated with an adequately powered cohort.

Using a power calculator (www.gigacalculator.com) it was determined that our sample size of 13 was one less than sufficient to detect a similar % difference in corticosterone as was detected in corticosterone. We regret that we unable to perform additional measurements as the author suggested in the available timeframe.

(2) All of the data throughout the MS (particularly data in the lung) should be presented in male and female mice. For example, the induction of ACE in the lungs of Marco-/- female mice should be absent. Similar concerns relate to the dexamethasone suppression studies. Also would be useful if the single cell data could be examined by sex--should be possible even post hoc using Xist etc.

Given the limitations outlined in our previous response to reviewers it was not possible to repeat every experiment from the original manuscript. We were able to measure the expression of lung Ace mRNA, ACE protein, adrenal weights, adrenal expression of steroid biosynthetic enzymes, presence of myeloid cells, and levels of serum electrolytes in female animals. These are presented in figures 1G, 3B, 4A, 4E, 4F, 4I, and 4J. We have elected to not present single cell seq data according to sex as it did not indicate substantial differences between males and females in Marco or Ace expression and so does not substantively change our approach.

(3) IF is notoriously unreliable in the lung, which has high levels of autofluorescence. This is the only method used to show ACE levels are increased in the absence of Marco. Orthogonal methods (e.g. immunoblots of flow-sorted cells, or ideally CITE-seq that includes both male and female mice) should be used.

We used negative controls to guide our settings during acquisition of immunofluorescent images. Additionally, we also used qPCR to show an increase in Ace mRNA expression in the lung in addition to the protein level. This data was presented in the original manuscript and is further bolstered by our additional presentation of expression data for Ace mRNA and protein in female animals in this revised manuscript.

(4) Given the central importance of ACE staining to the conclusions, validation of the antibody should be included in the supplement.

We don’t have ACE-deficient mice so cannot do KO validation of the antibody. We did perform secondary stain controls which confirmed the signal observed is primary antibody-derived. Moreover, we specifically chose an anti-ACE antibody (Invitrogen catalogue # MA5-32741) that has undergone advanced verification with the manufacturer. We additionally tested the antibody in the brain and liver and observed no significant levels of staining.

Author response image 1.

(5) The link between alveolar macrophage Marco and ACE is poorly explored.

We carried out a co-culture experiments of alveolar macrophages and endothelial cells and measure ACE/Ace expression as a consequence. This is presented in figure 5D and the discussion.

(6) Mechanisms explaining the substantial sex difference in the primary outcome are not explored.

This is outside the scope if this project, though we would consider exploring such experiments in future studies.

(7) Are there physiologic consequences either in homeostasis or under stress to the increased aldosterone (or lung ACE levels) observed in Marco-/- male mice?

We measured blood electrolytes and blood pressure in Marco-deficient and Marco-sufficient mice. The results from these experiments are presented in 4G-4M.

Reviewer #2 (Recommendations For The Authors):

Below is a suggestion of important control or validation experiments to be performed in order to support the authors' claims.

(1) It is imperative to validate that the phenotype observed in MARCO-deficient mice is indeed caused by the deficiency in MARCO. To this end, littermate mice issued from the crossing between heterozygous MARCO +/- mice should be compared to each other. C57BL/6J mice can first be crossed with MARCO-deficient mice in F0, and F1 heterozygous MARCO +/- mice should be crossed together to produce F2 MARCO +/+, MARCO +/- and MARCO -/- littermate mice that can be used for experiments.

We thank the reviewer for their comments. We recognise the concern of the reviewer but due to limited experimenter availability we are unable to undertake such a breeding programme to address this particular concern.

(2) The use of mice in which AM, but not other cells, lack MARCO expression would demonstrate that the effect is indeed linked to AM. To this end, AM-deficient Csf2rb-deficient mice could be adoptively transferred with MARCO-deficient AM. In addition, the phenotype of MARCO-deficient mice should be restored by the adoptive transfer of wild-type, MARCO-expressing AM. Alternatively, bone marrow chimeras in which only the hematopoietic compartment is deficient in MARCO would be another option, albeit less specific for AM.

We recognise the concern of the reviewer. We carried out a co-culture experiments of alveolar macrophages and endothelial cells and measure ACE/Ace expression as a consequence. This is presented in figure 5D and the implications explored in the discussion.

(3) If the hypothesis of the authors is correct, then additional read-outs could be performed to reinforce their claims: levels of Angiotensin I would be lower in MARCO-deficient mice, levels of Antiotensin II would be higher in MARCO-deficient mice, Arterial blood pressure would be higher in MARCO-deficient mice, natremia would be higher in MARCO-deficient mice, while kaliemia would be lower in MARCO-deficient mice. Similar read-outs could also be performed in the models proposed in point 2).

We measured blood electrolytes and blood pressure in Marco-deficient and Marco-sufficient mice. The results from these experiments are presented in 4G-4M.

(4) Co-culture experiments between MARCO-sufficient or deficient alveolar macrophages and lung endothelial cells, combined with the assessment of ACE expression, would allow the authors to evaluate whether the AM-expressed MARCO can directly regulate ACE expression.

To address this concern we carried out a co-culture experiment as described above.

Author response:

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

eLife Assessment

This useful study presents Altair-LSFM, a solid and well-documented implementation of a light-sheet fluorescence microscope (LSFM) designed for accessibility and cost reduction. While the approach offers strengths such as the use of custom-machined baseplates and detailed assembly instructions, its overall impact is limited by the lack of live-cell imaging capabilities and the absence of a clear, quantitative comparison to existing LSFM platforms. As such, although technically competent, the broader utility and uptake of this system by the community may be limited.

We thank the editors and reviewers for their thoughtful evaluation of our work and for recognizing the technical strengths of the Altair-LSFM platform, including the custom-machined baseplates and detailed documentation provided to promote accessibility and reproducibility. Below, we provide point-by-point responses to each referee comment. In the process, we have significantly revised the manuscript to include live-cell imaging data and a quantitative evaluation of imaging speed. We now more explicitly describe the different variants of lattice light-sheet microscopy—highlighting differences in their illumination flexibility and image acquisition modes—and clarify how Altair-LSFM compares to each. We further discuss challenges associated with the 5 mm coverslip and propose practical strategies to overcome them. Additionally, we outline cost-reduction opportunities, explain the rationale behind key equipment selections, and provide guidance for implementing environmental control. Altogether, we believe these additions have strengthened the manuscript and clarified both the capabilities and limitations of AltairLSFM.

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

The article presents the details of the high-resolution light-sheet microscopy system developed by the group. In addition to presenting the technical details of the system, its resolution has been characterized and its functionality demonstrated by visualizing subcellular structures in a biological sample.

Strengths: 

(1) The article includes extensive supplementary material that complements the information in the main article.

(2) However, in some sections, the information provided is somewhat superficial.

We thank the reviewer for their thoughtful assessment and for recognizing the strengths of our manuscript, including the extensive supplementary material. Our goal was to make the supplemental content as comprehensive and useful as possible. In addition to the materials provided with the manuscript, our intention is for the online documentation (available at thedeanlab.github.io/altair) to serve as a living resource that evolves in response to user feedback. We would therefore greatly appreciate the reviewer’s guidance on which sections were perceived as superficial so that we can expand them to better support readers and builders of the system.

Weaknesses:

(1) Although a comparison is made with other light-sheet microscopy systems, the presented system does not represent a significant advance over existing systems. It uses high numerical aperture objectives and Gaussian beams, achieving resolution close to theoretical after deconvolution. The main advantage of the presented system is its ease of construction, thanks to the design of a perforated base plate.

We appreciate the reviewer’s assessment and the opportunity to clarify our intent. Our primary goal was not to introduce new optical functionality beyond that of existing high-performance light-sheet systems, but rather to substantially reduce the barrier to entry for non-specialist laboratories. Many open-source implementations, such as OpenSPIM, OpenSPIN, and Benchtop mesoSPIM, similarly focused on accessibility and reproducibility rather than introducing new optical modalities, yet have had a measureable impact on the field by enabling broader community participation. Altair-LSFM follows this tradition, providing sub-cellular resolution performance comparable to advanced systems like LLSM, while emphasizing reproducibility, ease of construction through a precision-machined baseplate, and comprehensive documentation to facilitate dissemination and adoption.

(2) Using similar objectives (Nikon 25x and Thorlabs 20x), the results obtained are similar to those of the LLSM system (using a Gaussian beam without laser modulation). However, the article does not mention the difficulties of mounting the sample in the implemented configuration.

We appreciate the reviewer’s comment and agree that there are practical challenges associated with handling 5 mm diameter coverslips in this configuration. In the revised manuscript, we now explicitly describe these challenges and provide practical solutions. Specifically, we highlight the use of a custommachined coverslip holder designed to simplify mounting and handling, and we direct readers to an alternative configuration using the Zeiss W Plan-Apochromat 20×/1.0 objective, which eliminates the need for small coverslips altogether.

(3) The authors present a low-cost, open-source system. Although they provide open source code for the software (navigate), the use of proprietary electronics (ASI, NI, etc.) makes the system relatively expensive. Its low cost is not justified.

We appreciate the reviewer’s perspective and understand the concern regarding the use of proprietary control hardware such as the ASI Tiger Controller and NI data acquisition cards. Our decision to use these components was intentional: relying on a unified, professionally supported and maintained platform minimizes complexity associated with sourcing, configuring, and integrating hardware from multiple vendors, thereby reducing non-financial barriers to entry for non-specialist users.

Importantly, these components are not the primary cost driver of Altair-LSFM (they represent roughly 18% of the total system cost). Nonetheless, for individuals where the price is prohibitive, we also outline several viable cost-reduction options in the revised manuscript (e.g., substituting manual stages, omitting the filter wheel, or using industrial CMOS cameras), while discussing the trade-offs these substitutions introduce in performance and usability. These considerations are now summarized in Supplementary Note 1, which provides a transparent rationale for our design and cost decisions.

Finally, we note that even with these professional-grade components, Altair-LSFM remains substantially less expensive than commercial systems offering comparable optical performance, such as LLSM implementations from Zeiss or 3i.

(4) The fibroblast images provided are of exceptional quality. However, these are fixed samples. The system lacks the necessary elements for monitoring cells in vivo, such as temperature or pH control.

We thank the reviewer for their positive comment regarding the quality of our data. As noted, the current manuscript focuses on validating the optical performance and resolution of the system using fixed specimens to ensure reproducibility and stability.

We fully agree on the importance of environmental control for live-cell imaging. In the revised manuscript, we now describe in detail how temperature regulation can be achieved using a custom-designed heated sample chamber, accompanied by detailed assembly instructions on our GitHub repository and summarized in Supplementary Note 2. For pH stabilization in systems lacking a 5% CO₂ atmosphere, we recommend supplementing the imaging medium with 10–25 mM HEPES buffer. Additionally, we include new live-cell imaging data demonstrating that Altair-LSFM supports in vitro time-lapse imaging of dynamic cellular processes under controlled temperature conditions.

Reviewer #2 (Public review): 

Summary: 

The authors present Altair-LSFM (Light Sheet Fluorescence Microscope), a high-resolution, open-source microscope, that is relatively easy to align and construct and achieves sub-cellular resolution. The authors developed this microscope to fill a perceived need that current open-source systems are primarily designed for large specimens and lack sub-cellular resolution or are difficult to construct and align, and are not stable. While commercial alternatives exist that offer sub-cellular resolution, they are expensive. The authors' manuscript centers around comparisons to the highly successful lattice light-sheet microscope, including the choice of detection and excitation objectives. The authors thus claim that there remains a critical need for high-resolution, economical, and easy-to-implement LSFM systems. 

We thank the reviewer for their thoughtful summary. We agree that existing open-source systems primarily emphasize imaging of large specimens, whereas commercial systems that achieve sub-cellular resolution remain costly and complex. Our aim with Altair-LSFM was to bridge this gap—providing LLSM-level performance in a substantially more accessible and reproducible format. By combining high-NA optics with a precision-machined baseplate and open-source documentation, Altair offers a practical, high-resolution solution that can be readily adopted by non-specialist laboratories.

Strengths: 

The authors succeed in their goals of implementing a relatively low-cost (~ USD 150K) open-source microscope that is easy to align. The ease of alignment rests on using custom-designed baseplates with dowel pins for precise positioning of optics based on computer analysis of opto-mechanical tolerances, as well as the optical path design. They simplify the excitation optics over Lattice light-sheet microscopes by using a Gaussian beam for illumination while maintaining lateral and axial resolutions of 235 and 350 nm across a 260-um field of view after deconvolution. In doing so they rest on foundational principles of optical microscopy that what matters for lateral resolution is the numerical aperture of the detection objective and proper sampling of the image field on to the detection, and the axial resolution depends on the thickness of the light-sheet when it is thinner than the depth of field of the detection objective. This concept has unfortunately not been completely clear to users of high-resolution light-sheet microscopes and is thus a valuable demonstration. The microscope is controlled by an open-source software, Navigate, developed by the authors, and it is thus foreseeable that different versions of this system could be implemented depending on experimental needs while maintaining easy alignment and low cost. They demonstrate system performance successfully by characterizing their sheet, point-spread function, and visualization of sub-cellular structures in mammalian cells, including microtubules, actin filaments, nuclei, and the Golgi apparatus.

We thank the reviewer for their thoughtful and generous assessment of our work. We are pleased that the manuscript’s emphasis on fundamental optical principles, design rationale, and practical implementation was clearly conveyed. We agree that Altair’s modular and accessible architecture provides a strong foundation for future variants tailored to specific experimental needs. To facilitate this, we have made all Zemax simulations, CAD files, and build documentation openly available on our GitHub repository, enabling users to adapt and extend the system for diverse imaging applications.

Weaknesses:

There is a fixation on comparison to the first-generation lattice light-sheet microscope, which has evolved significantly since then:

(1) The authors claim that commercial lattice light-sheet microscopes (LLSM) are "complex, expensive, and alignment intensive", I believe this sentence applies to the open-source version of LLSM, which was made available for wide dissemination. Since then, a commercial solution has been provided by 3i, which is now being used in multiple cores and labs but does require routine alignments. However, Zeiss has also released a commercial turn-key system, which, while expensive, is stable, and the complexity does not interfere with the experience of the user. Though in general, statements on ease of use and stability might be considered anecdotal and may not belong in a scientific article, unreferenced or without data.

We thank the reviewer for this thoughtful and constructive comment. We have revised the manuscript to more clearly distinguish between the original open-source implementation of LLSM and subsequent commercial versions by 3i and ZEISS. The revised Introduction and Discussion now explicitly note that while open-source and early implementations of LLSM can require expert alignment and maintenance, commercial systems—particularly the ZEISS Lattice Lightsheet 7—are designed for automated operation and stable, turn-key use, albeit at higher cost and with limited modifiability. We have also moderated earlier language regarding usability and stability to avoid anecdotal phrasing.

We also now provide a more objective proxy for system complexity: the number of optical elements that require precise alignment during assembly and maintenance thereafter. The original open-source LLSM setup includes approximately 29 optical components that must each be carefully positioned laterally, angularly, and coaxially along the optical path. In contrast, the first-generation Altair-LSFM system contains only nine such elements. By this metric, Altair-LSFM is considerably simpler to assemble and align, supporting our overarching goal of making high-resolution light-sheet imaging more accessible to non-specialist laboratories.

(2) One of the major limitations of the first generation LLSM was the use of a 5 mm coverslip, which was a hinderance for many users. However, the Zeiss system elegantly solves this problem, and so does Oblique Plane Microscopy (OPM), while the Altair-LSFM retains this feature, which may dissuade widespread adoption. This limitation and how it may be overcome in future iterations is not discussed.

We thank the reviewer for this helpful comment. We agree that the use of 5 mm diameter coverslips, while enabling high-NA imaging in the current Altair-LSFM configuration, may pose a practical limitation for some users. We now discuss this more explicitly in the revised manuscript. Specifically, we note that replacing the detection objective provides a straightforward solution to this constraint. For example, as demonstrated by Moore et al. (Lab Chip, 2021), pairing the Zeiss W Plan-Apochromat 20×/1.0 detection objective with the Thorlabs TL20X-MPL illumination objective allows imaging beyond the physical surfaces of both objectives, eliminating the need for small-format coverslips. In the revised text, we propose this modification as an accessible path toward greater compatibility with conventional sample mounting formats. We also note in the Discussion that Oblique Plane Microscopy (OPM) inherently avoids such nonstandard mounting requirements and, owing to its single-objective architecture, is fully compatible with standard environmental chambers.

(3) Further, on the point of sample flexibility, all generations of the LLSM, and by the nature of its design, the OPM, can accommodate live-cell imaging with temperature, gas, and humidity control. It is unclear how this would be implemented with the current sample chamber. This limitation would severely limit use cases for cell biologists, for which this microscope is designed. There is no discussion on this limitation or how it may be overcome in future iterations.

We thank the reviewer for this important observation and agree that environmental control is critical for live-cell imaging applications. It is worth noting that the original open-source LLSM design, as well as the commercial version developed by 3i, provided temperature regulation but did not include integrated control of CO2 or humidity. Despite this limitation, these systems have been widely adopted and have generated significant biological insights. We also acknowledge that both OPM and the ZEISS implementation of LLSM offer clear advantages in this respect, providing compatibility with standard commercial environmental chambers that support full regulation of temperature, CO₂, and humidity.

In the revised manuscript, we expand our discussion of environmental control in Supplementary Note 2, where we describe the Altair-LSFM chamber design in more detail and discuss its current implementation of temperature regulation and HEPES-based pH stabilization. Additionally, the Discussion now explicitly notes that OPM avoids the challenges associated with non-standard sample mounting and is inherently compatible with conventional environmental enclosures.

(4) The authors' comparison to LLSM is constrained to the "square" lattice, which, as they point out, is the most used optical lattice (though this also might be considered anecdotal). The LLSM original design, however, goes far beyond the square lattice, including hexagonal lattices, the ability to do structured illumination, and greater flexibility in general in terms of light-sheet tuning for different experimental needs, as well as not being limited to just sample scanning. Thus, the Alstair-LSFM cannot compare to the original LLSM in terms of versatility, even if comparisons to the resolution provided by the square lattice are fair.

We agree that the original LLSM design offers substantially greater flexibility than what is reflected in our initial comparison, including the ability to generate multiple lattice geometries (e.g., square and hexagonal), operate in structured illumination mode, and acquire volumes using both sample- and lightsheet–scanning strategies. To address this, we now include Supplementary Note 3 that provides a detailed overview of the illumination modes and imaging flexibility afforded by the original LLSM implementation, and how these capabilities compare to both the commercial ZEISS Lattice Lightsheet 7 and our AltairLSFM system. In addition, we have revised the discussion to explicitly acknowledge that the original LLSM could operate in alternative scan strategies beyond sample scanning, providing greater context for readers and ensuring a more balanced comparison.

(5) There is no demonstration of the system's live-imaging capabilities or temporal resolution, which is the main advantage of existing light-sheet systems.

In the revised manuscript, we now include a demonstration of live-cell imaging to directly validate AltairLSFM’s suitability for dynamic biological applications. We also explicitly discuss the temporal resolution of the system in the main text (see Optoelectronic Design of Altair-LSFM), where we detail both software- and hardware-related limitations. Specifically, we evaluate the maximum imaging speed achievable with Altair-LSFM in conjunction with our open-source control software, navigate.

For simplicity and reduced optoelectronic complexity, the current implementation powers the piezo through the ASI Tiger Controller, which modestly reduces its bandwidth. Nonetheless, for a 100 µm stroke typical of light-sheet imaging, we achieved sufficient performance to support volumetric imaging at most biologically relevant timescales. These results, along with additional discussion of the design trade-offs and performance considerations, are now included in the revised manuscript and expanded upon in the supplementary material.

While the microscope is well designed and completely open source, it will require experience with optics, electronics, and microscopy to implement and align properly. Experience with custom machining or soliciting a machine shop is also necessary. Thus, in my opinion, it is unlikely to be implemented by a lab that has zero prior experience with custom optics or can hire someone who does. Altair-LSFM may not be as easily adaptable or implementable as the authors describe or perceive in any lab that is interested, even if they can afford it. The authors indicate they will offer "workshops," but this does not necessarily remove the barrier to entry or lower it, perhaps as significantly as the authors describe.

We appreciate the reviewer’s perspective and agree that building any high-performance custom microscope—Altair-LSFM included—requires a basic understanding of (or willingness to learn) optics, electronics, and instrumentation. Such a barrier exists for all open-source microscopes, and our goal is not to eliminate this requirement entirely but to substantially reduce the technical and logistical challenges that typically accompany the construction of custom light-sheet systems.

Importantly, no machining experience or in-house fabrication capabilities are required. Users can simply submit the provided CAD design files and specifications directly to commercial vendors for fabrication. We have made this process as straightforward as possible by supplying detailed build instructions, recommended materials, and vendor-ready files through our GitHub repository. Our dissemination strategy draws inspiration from other successful open-source projects such as mesoSPIM, which has seen widespread adoption—over 30 implementations worldwide—through a similar model of exhaustive documentation, open-source software, and community support via user meetings and workshops.

We also recognize that documentation alone cannot fully replace hands-on experience. To further lower barriers to adoption, we are actively working with commercial vendors to streamline procurement and assembly, and Altair-LSFM is supported by a Biomedical Technology Development and Dissemination (BTDD) grant that provides resources for hosting workshops, offering real-time community support, and developing supplementary training materials.

In the revised manuscript, we now expand the Discussion to explicitly acknowledge these implementation considerations and to outline our ongoing efforts to support a broad and diverse user base, ensuring that laboratories with varying levels of technical expertise can successfully adopt and maintain the Altair-LSFM platform.

There is a claim that this design is easily adaptable. However, the requirement of custom-machined baseplates and in silico optimization of the optical path basically means that each new instrument is a new design, even if the Navigate software can be used. It is unclear how Altair-LSFM demonstrates a modular design that reduces times from conception to optimization compared to previous implementations.

We thank the reviewer for this insightful comment and agree that our original language regarding adaptability may have overstated the degree to which Altair-LSFM can be modified without prior experience. It was not our intention to imply that the system can be easily redesigned by users with limited technical background. Meaningful adaptations of the optical or mechanical design do require expertise in optical layout, optomechanical design, and alignment.

That said, for laboratories with such expertise, we aim to facilitate modifications by providing comprehensive resources—including detailed Zemax simulations, complete CAD models, and alignment documentation. These materials are intended to reduce the development burden for expert users seeking to tailor the system to specific experimental requirements, without necessitating a complete re-optimization of the optical path from first principles.

In the revised manuscript, we clarify this point and temper our language regarding adaptability to better reflect the realistic scope of customization. Specifically, we now state in the Discussion: “For expert users who wish to tailor the instrument, we also provide all Zemax illumination-path simulations and CAD files, along with step-by-step optimization protocols, enabling modification and re-optimization of the optical system as needed.” This revision ensures that readers clearly understand that Altair-LSFM is designed for reproducibility and straightforward assembly in its default configuration, while still offering the flexibility for modification by experienced users.

Reviewer #3 (Public review):

Summary: 

This manuscript introduces a high-resolution, open-source light-sheet fluorescence microscope optimized for sub-cellular imaging. The system is designed for ease of assembly and use, incorporating a custommachined baseplate and in silico optimized optical paths to ensure robust alignment and performance. The authors demonstrate lateral and axial resolutions of ~235 nm and ~350 nm after deconvolution, enabling imaging of sub-diffraction structures in mammalian cells. The important feature of the microscope is the clever and elegant adaptation of simple gaussian beams, smart beam shaping, galvo pivoting and high NA objectives to ensure a uniform thin light-sheet of around 400 nm in thickness, over a 266 micron wide Field of view, pushing the axial resolution of the system beyond the regular diffraction limited-based tradeoffs of light-sheet fluorescence microscopy. Compelling validation using fluorescent beads and multicolor cellular imaging highlights the system's performance and accessibility. Moreover, a very extensive and comprehensive manual of operation is provided in the form of supplementary materials. This provides a DIY blueprint for researchers who want to implement such a system.

We thank the reviewer for their thoughtful and positive assessment of our work. We appreciate their recognition of Altair-LSFM’s design and performance, including its ability to achieve high-resolution, imaging throughout a 266-micron field of view. While Altair-LSFM approaches the practical limits of diffraction-limited performance, it does not exceed the fundamental diffraction limit; rather, it achieves near-theoretical resolution through careful optical optimization, beam shaping, and alignment. We are grateful for the reviewer’s acknowledgment of the accessibility and comprehensive documentation that make this system broadly implementable.

Strengths:

(1) Strong and accessible technical innovation: With an elegant combination of beam shaping and optical modelling, the authors provide a high-resolution light-sheet system that overcomes the classical light-sheet tradeoff limit of a thin light-sheet and a small field of view. In addition, the integration of in silico modelling with a custom-machined baseplate is very practical and allows for ease of alignment procedures. Combining these features with the solid and super-extensive guide provided in the supplementary information, this provides a protocol for replicating the microscope in any other lab.

(2) Impeccable optical performance and ease of mounting of samples: The system takes advantage of the same sample-holding method seen already in other implementations, but reduces the optical complexity.

At the same time, the authors claim to achieve similar lateral and axial resolution to Lattice-light-sheet microscopy (although without a direct comparison (see below in the "weaknesses" section). The optical characterization of the system is comprehensive and well-detailed. Additionally, the authors validate the system imaging sub-cellular structures in mammalian cells.

(3) Transparency and comprehensiveness of documentation and resources: A very detailed protocol provides detailed documentation about the setup, the optical modeling, and the total cost.

We thank the reviewer for their thoughtful and encouraging comments. We are pleased that the technical innovation, optical performance, and accessibility of Altair-LSFM were recognized. Our goal from the outset was to develop a diffraction-limited, high-resolution light-sheet system that balances optical performance with reproducibility and ease of implementation. We are also pleased that the use of precisionmachined baseplates was recognized as a practical and effective strategy for achieving performance while maintaining ease of assembly.

Weaknesses: 

(1) Limited quantitative comparisons: Although some qualitative comparison with previously published systems (diSPIM, lattice light-sheet) is provided throughout the manuscript, some side-by-side comparison would be of great benefit for the manuscript, even in the form of a theoretical simulation. While having a direct imaging comparison would be ideal, it's understandable that this goes beyond the interest of the paper; however, a table referencing image quality parameters (taken from the literature), such as signalto-noise ratio, light-sheet thickness, and resolutions, would really enhance the features of the setup presented. Moreover, based also on the necessity for optical simplification, an additional comment on the importance/difference of dual objective/single objective light-sheet systems could really benefit the discussion.

In the revised manuscript, we have significantly expanded our discussion of different light-sheet systems to provide clearer quantitative and conceptual context for Altair-LSFM. These comparisons are based on values reported in the literature, as we do not have access to many of these instruments (e.g., DaXi, diSPIM, or commercial and open-source variants of LLSM), and a direct experimental comparison is beyond the scope of this work.

We note that while quantitative parameters such as signal-to-noise ratio are important, they are highly sample-dependent and strongly influenced by imaging conditions, including fluorophore brightness, camera characteristics, and filter bandpass selection. For this reason, we limited our comparison to more general image-quality metrics—such as light-sheet thickness, resolution, and field of view—that can be reliably compared across systems.

Finally, per the reviewer’s recommendation, we have added additional discussion clarifying the differences between dual-objective and single-objective light-sheet architectures, outlining their respective strengths, limitations, and suitability for different experimental contexts.

(2) Limitation to a fixed sample: In the manuscript, there is no mention of incubation temperature, CO₂ regulation, Humidity control, or possible integration of commercial environmental control systems. This is a major limitation for an imaging technique that owes its popularity to fast, volumetric, live-cell imaging of biological samples.

We fully agree that environmental control is critical for live-cell imaging applications. In the revised manuscript, we now describe the design and implementation of a temperature-regulated sample chamber in Supplementary Note 2, which maintains stable imaging conditions through the use of integrated heating elements and thermocouples. This approach enables precise temperature control while minimizing thermal gradients and optical drift. For pH stabilization, we recommend the use of 10–25 mM HEPES in place of CO₂ regulation, consistent with established practice for most light-sheet systems, including the initial variant of LLSM. Although full humidity and CO₂ control are not readily implemented in dual-objective configurations, we note that single-objective designs such as OPM are inherently compatible with commercial environmental chambers and avoid these constraints. Together, these additions clarify how environmental control can be achieved within Altair-LSFM and situate its capabilities within the broader LSFM design space.

(3) System cost and data storage cost: While the system presented has the advantage of being opensource, it remains relatively expensive (considering the 150k without laser source and optical table, for example). The manuscript could benefit from a more direct comparison of the performance/cost ratio of existing systems, considering academic settings with budgets that most of the time would not allow for expensive architectures. Moreover, it would also be beneficial to discuss the adaptability of the system, in case a 30k objective could not be feasible. Will this system work with different optics (with the obvious limitations coming with the lower NA objective)? This could be an interesting point of discussion. Adaptability of the system in case of lower budgets or more cost-effective choices, depending on the needs.

We agree that cost considerations are critical for adoption in academic environments. We would also like to clarify that the quoted $150k includes the optical table and laser source. In the revised manuscript, Supplementary Note 1 now includes an expanded discussion of cost–performance trade-offs and potential paths for cost reduction.

Last, not much is said about the need for data storage. Light-sheet microscopy's bottleneck is the creation of increasingly large datasets, and it could be beneficial to discuss more about the storage needs and the quantity of data generated.

In the revised manuscript, we now include Supplementary Note 4, which provides a high-level discussion of data storage needs, approximate costs, and practical strategies for managing large datasets generated by light-sheet microscopy. This section offers general guidance—including file-format recommendations, and cost considerations—but we note that actual costs will vary by institution and contractual agreements.

Conclusion:

Altair-LSFM represents a well-engineered and accessible light-sheet system that addresses a longstanding need for high-resolution, reproducible, and affordable sub-cellular light-sheet imaging. While some aspects-comparative benchmarking and validation, limitation for fixed samples-would benefit from further development, the manuscript makes a compelling case for Altair-LSFM as a valuable contribution to the open microscopy scientific community. 

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) A picture, or full CAD design of the complete instrument, should be included as a main figure.

A complete CAD rendering of the microscope is now provided in Supplementary Figure 4.

(2) There is no quantitative comparison of the effects of the tilting resonant galvo; only a cartoon, a figure should be included.

The cartoon was intended purely as an educational illustration to conceptually explain the role of the tilting resonant galvo in shaping and homogenizing the light sheet. To clarify this intent, we have revised both the figure legend and corresponding text in the main manuscript. For readers seeking quantitative comparisons, we now reference the original study that provides a detailed analysis of this optical approach, as well as a review on the subject.

(3) Description of L4 is missing in the Figure 1 caption.

Thank you for catching this omission. We have corrected it.

(4) The beam profiles in Figures 1c and 3a, please crop and make the image bigger so the profile can be appreciated. The PSFs in Figure 3c-e should similarly be enlarged and presented using a dynamic range/LUT such that any aberrations can be appreciated.

In Figure 1c, our goal was to qualitatively illustrate the uniformity of the light-sheet across the full field of view, while Figure 1d provided the corresponding quantitative cross-section. To improve clarity, we have added an additional figure panel offering a higher-magnification, localized view of the light-sheet profile. For Figure 3c–e, we have enlarged the PSF images and adjusted the display range to better convey the underlying signal and allow subtle aberrations to be appreciated.

(5) It is unclear why LLSM is being used as the gold standard, since in its current commercial form, available from Zeiss, it is a turn-key system designed for core facilities. The original LLSM is also a versatile instrument that provides much more than the square lattice for illumination, including structured illumination, hexagonal lattices, live-cell imaging, wide-field illumination, different scan modes, etc. These additional features are not even mentioned when compared to the Altair-LSFM. If a comparison is to be provided, it should be fair and balanced. Furthermore, as outlined in the public review, anecdotal statements on "most used", "difficult to align", or "unstable" should not be provided without data.

In the revised manuscript, we have carefully removed anecdotal statements and, where appropriate, replaced them with quantitative or verifiable information. For instance, we now explicitly report that the square lattice was used in 16 of the 20 figure subpanels in the original LLSM publication, and we include a proxy for optical complexity based on the number of optical elements requiring alignment in each system.

We also now clearly distinguish between the original LLSM design—which supports multiple illumination and scanning modes—and its subsequent commercial variants, including the ZEISS Lattice Lightsheet 7, which prioritizes stability and ease of use over configurational flexibility (see Supplementary Note 3).

(6) The authors should recognize that implementing custom optics, no matter how well designed, is a big barrier to cross for most cell biology labs.

We fully understand and now acknowledge in the main text that implementing custom optics can present a significant barrier, particularly for laboratories without prior experience in optical system assembly. However, similar challenges were encountered during the adoption of other open-source microscopy platforms, such as mesoSPIM and OpenSPIM, both of which have nonetheless achieved widespread implementation. Their success has largely been driven by exhaustive documentation, strong community support, and standardized design principles—approaches we have also prioritized in Altair-LSFM. We have therefore made all CAD files, alignment guides, and detailed build documentation publicly available and continue to develop instructional materials and community resources to further reduce the barrier to adoption.

(7) Statements on "hands on workshops" though laudable, may not be appropriate to include in a scientific publication without some documentation on the influence they have had on implanting the microscope.

We understand the concern. Our intention in mentioning hands-on workshops was to convey that the dissemination effort is supported by an NIH Biomedical Technology Development and Dissemination grant, which includes dedicated channels for outreach and community engagement. Nonetheless, we agree that such statements are not appropriate without formal documentation of their impact, and we have therefore removed this text from the revised manuscript.

(8) It is claimed that the microscope is "reliable" in the discussion, but with no proof, long-term stability should be assessed and included.

Our experience with Altair-LSFM has been that it remains well-aligned over time—especially in comparison to other light-sheet systems we worked on throughout the last 11 years—we acknowledge that this assessment is anecdotal. As such, we have omitted this claim from the revised manuscript.

(9) Due to the reliance on anecdotal statements and comparisons without proof to other systems, this paper at times reads like a brochure rather than a scientific publication. The authors should consider editing their manuscript accordingly to focus on the technical and quantifiable aspects of their work.

We agree with the reviewer’s assessment and have revised the manuscript to remove anecdotal comparisons and subjective language. Where possible, we now provide quantitative metrics or verifiable data to support our statements.

Reviewer #3 (Recommendations for the authors):

Other minor points that could improve the manuscript (although some of these points are explained in the huge supplementary manual): 

(1) The authors explain thoroughly their design, and they chose a sample-scanning method. I think that a brief discussion of the advantages and disadvantages of such a method over, for example, a laserscanning system (with fixed sample) in the main text will be highly beneficial for the users.

In the revised manuscript, we now include a brief discussion in the main text outlining the advantages and limitations of a sample-scanning approach relative to a light-sheet–scanning system. Specifically, we note that for thin, adherent specimens, sample scanning minimizes the optical path length through the sample, allowing the use of more tightly focused illumination beams that improve axial resolution. We also include a new supplementary figure illustrating how this configuration reduces the propagation length of the illumination light sheet, thereby enhancing axial resolution.

(2) The authors justify selecting a 0.6 NA illumination objective over alternatives (e.g., Special Optics), but the manuscript would benefit from a more quantitative trade-off analysis (beam waist, working distance, sample compatibility) with other possibilities. Within the objective context, a comparison of the performances of this system with the new and upcoming single-objective light-sheet methods (and the ones based also on optical refocusing, e.g., DAXI) would be very interesting for the goodness of the manuscript.

In the revised manuscript, we now provide a quantitative trade-off analysis of the illumination objectives in Supplementary Note 1, including comparisons of beam waist, working distance, and sample compatibility. This section also presents calculated point spread functions for both the 0.6 NA and 0.67 NA objectives, outlining the performance trade-offs that informed our design choice. In addition, Supplementary Note 3 now includes a broader comparison of Altair-LSFM with other light-sheet modalities, including diSPIM, ASLM, and OPM, to further contextualize the system’s capabilities within the evolving light-sheet microscopy landscape.

(3) The modularity of the system is implied in the context of the manuscript, but not fully explained. The authors should specify more clearly, for example, if cameras could be easily changed, objectives could be easily swapped, light-sheet thickness could be tuned by changing cylindrical lens, how users might adapt the system for different samples (e.g., embryos, cleared tissue, live imaging), .etc, and discuss eventual constraints or compatibility issues to these implementations.

Altair-LSFM was explicitly designed and optimized for imaging live adherent cells, where sample scanning and short light-sheet propagation lengths provide optimal axial resolution (Supplementary Note 3). While the same platform could be used for superficial imaging in embryos, systems implementing multiview illumination and detection schemes are better suited for such specimens. Similarly, cleared tissue imaging typically requires specialized solvent-compatible objectives and approaches such as ASLM that maximize the field of view. We have now added some text to the Design Principles section that explicitly state this.

Altair-LSFM offers varying levels of modularity depending on the user’s level of expertise. For entry-level users, the illumination numerical aperture—and therefore the light-sheet thickness and propagation length—can be readily adjusted by tuning the rectangular aperture conjugate to the back pupil of the illumination objective, as described in the Design Principles section. For mid-level users, alternative configurations of Altair-LSFM, including different detection objectives, stages, filter wheels, or cameras, can be readily implemented (Supplementary Note 1). Importantly, navigate natively supports a broad range of hardware devices, and new components can be easily integrated through its modular interface. For expert users, all Zemax simulations, CAD models, and step-by-step optimization protocols are openly provided, enabling complete re-optimization of the optical design to meet specific experimental requirements.

(4) Resolution measurements before and after deconvolution are central to the performance claim, but the deconvolution method (PetaKit5D) is only briefly mentioned in the main text, it's not referenced, and has to be clarified in more detail, coherently with the precision of the supplementary information. More specifically, PetaKit5D should be referenced in the main text, the details of the deconvolution parameters discussed in the Methods section, and the computational requirements should also be mentioned. 

In the revised manuscript, we now provide a dedicated description of the deconvolution process in the Methods section, including the specific parameters and algorithms used. We have also explicitly referenced PetaKit5D in the main text to ensure proper attribution and clarity. Additionally, we note the computational requirements associated with this analysis in the same section for completeness.

(5)  Image post-processing is not fully explained in the main text. Since the system is sample-scanning based, no word in the main text is spent on deskewing, which is an integral part of the post-processing to obtain a "straight" 3D stack. Since other systems implement such a post-processing algorithm (for example, single-objective architectures), it would be beneficial to have some discussion about this, and also a brief comparison to other systems in the main text in the methods section. 

In the revised manuscript, we now explicitly describe both deskewing (shearing) and deconvolution procedures in the Alignment and Characterization section of the main text and direct readers to the Methods section. We also briefly explain why the data must be sheared to correct for the angled sample-scanning geometry for LLSM and Altair-LSFM, as well as both sample-scanning and laser-scanning-variants of OPMs.

(6) A brief discussion on comparative costs with other systems (LLSM, dispim, etc.) could be helpful for non-imaging expert researchers who could try to implement such an optical architecture in their lab.

Unfortunately, the exact costs of commercial systems such as LLSM or diSPIM are typically not publicly available, as they depend on institutional agreements and vendor-specific quotations. Nonetheless, we now provide approximate cost estimates in Supplementary Note 1 to help readers and prospective users gauge the expected scale of investment relative to other advanced light-sheet microscopy systems.

(7) The "navigate" control software is provided, but a brief discussion on its advantages compared to an already open-access system, such as Micromanager, could be useful for the users.

In the revised manuscript, we now include Supplementary Note 5 that discusses the advantages and disadvantages of different open-source microscope control platforms, including navigate and MicroManager. In brief, navigate was designed to provide turnkey support for multiple light-sheet architectures, with pre-configured acquisition routines optimized for Altair-LSFM, integrated data management with support for multiple file formats (TIFF, HDF5, N5, and Zarr), and full interoperability with OMEcompliant workflows. By contrast, while Micro-Manager offers a broader library of hardware drivers, it typically requires manual configuration and custom scripting for advanced light-sheet imaging workflows.

(8) The cost and parts are well documented, but the time and expertise required are not crystal clear.Adding a simple time estimate (perhaps in the Supplement Section) of assembly/alignment/installation/validation and first imaging will be very beneficial for users. Also, what level of expertise is assumed (prior optics experience, for example) to be needed to install a system like this? This can help non-optics-expert users to better understand what kind of adventure they are putting themselves through.

We thank the reviewer for this helpful suggestion. To address this, we have added Supplementary Table S5, which provides approximate time estimates for assembly, alignment, validation, and first imaging based on the user’s prior experience with optical systems. The table distinguishes between novice (no prior experience), moderate (some experience using but not assembling optical systems), and expert (experienced in building and aligning optical systems) users. This addition is intended to give prospective builders a realistic sense of the time commitment and level of expertise required to assemble and validate AltairLSFM.

Minor things in the main text:

(1) Line 109: The cost is considered "excluding the laser source". But then in the table of costs, you mention L4cc as a "multicolor laser source", for 25 K. Can you explain this better? Are the costs correct with or without the laser source? 

We acknowledge that the statement in line 109 was incorrect—the quoted ~$150k system cost does include the laser source (L4cc, listed at $25k in the cost table). We have corrected this in the revised manuscript.

(2) Line 113: You say "lateral resolution, but then you state a 3D resolution (230 nm x 230 nm x 370 nm). This needs to be fixed.

Thank you, we have corrected this.

(3) Line 138: Is the light-sheet uniformity proven also with a fluorescent dye? This could be beneficial for the main text, showing the performance of the instrument in a fluorescent environment.

The light-sheet profiles shown in the manuscript were acquired using fluorescein to visualize the beam. We have revised the main text and figure legends to clearly state this.

(4) Line 149: This is one of the most important features of the system, defying the usual tradeoff between light-sheet thickness and field of view, with a regular Gaussian beam. I would clarify more specifically how you achieve this because this really is the most powerful takeaway of the paper.

We thank the reviewer for this key observation. The ability of Altair-LSFM to maintain a thin light sheet across a large field of view arises from diffraction effects inherent to high NA illumination. Specifically, diffraction elongates the PSF along the beam’s propagation direction, effectively extending the region over which the light sheet remains sufficiently thin for high-resolution imaging. This phenomenon, which has been the subject of active discussion within the light-sheet microscopy community, allows Altair-LSFM to partially overcome the conventional trade-off between light-sheet thickness and propagation length. We now clarify this point in the main text and provide a more detailed discussion in Supplementary Note 3, which is explicitly referenced in the discussion of the revised manuscript.

(5) Line 171: You talk about repeatable assembly...have you tried many different baseplates? Otherwise, this is a complicated statement, since this is a proof-of-concept paper. 

We thank the reviewer for this comment. We have not yet validated the design across multiple independently assembled baseplates and therefore agree that our previous statement regarding repeatable assembly was premature. To avoid overstating the current level of validation, we have removed this statement from the revised manuscript.

(6) Line 187: same as above. You mention "long-term stability". For how long did you try this? This should be specified in numbers (days, weeks, months, years?) Otherwise, it is a complicated statement to make, since this is a proof-of-concept paper.

We also agree that referencing long-term stability without quantitative backing is inappropriate, and have removed this statement from the revised manuscript.

(7) Line 198: "rapid z-stack acquisition. How rapid? Also, what is the limitation of the galvo-scanning in terms of the imaging speed of the system? This should be noted in the methods section.

In the revised manuscript, we now clarify these points in the Optoelectronic Design section. Specifically, we explicitly note that the resonant galvo used for shadow reduction operates at 4 kHz, ensuring that it is not rate-limiting for any imaging mode. In the same section, we also evaluate the maximum acquisition speeds achievable using navigate and report the theoretical bandwidth of the sample-scanning piezo, which together define the practical limits of volumetric acquisition speed for Altair-LSFM.

(8) Line 234: Peta5Kit is discussed in the additional documentation, but should be referenced here, as well.

We now reference and cite PetaKit5D.

(9) Line 256: "values are on par with LLSM", but no values are provided. Some details should also be provided in the main text.

In the revised manuscript, we now provide the lateral and axial resolution values originally reported for LLSM in the main text to facilitate direct comparison with Altair-LSFM. Additionally, Supplementary Note 3 now includes an expanded discussion on the nuances of resolution measurement and reporting in lightsheet microscopy.

Figures:

(1) Figure 1 could be implemented with Figure 3. They're both discussing the validation of the system (theoretically and with simulations), and they could be together in different panels of the same figure. The experimental light-sheet seems to be shown in a transmission mode. Showing a pattern in a fluorescent dye could also be beneficial for the paper.

In Figure 1, our goal was to guide readers through the design process—illustrating how the detection objective’s NA sets the system’s resolution, which defines the required pixel size for Nyquist sampling and, in turn, the field of view. We then use Figure 1b–c to show how the illumination beam was designed and simulated to achieve that field of view. In contrast, Figure 3 presents the experimental validation of the illumination system. To avoid confusion, we now clarify in the text that the light sheet shown in Figure 3 was visualized in a fluorescein solution and imaged in transmission mode. While we agree that Figures 1 and 3 both serve to validate the system, we prefer to keep them as separate figures to maintain focus within each panel. We believe this organization better supports the narrative structure and allows readers to digest the theoretical and experimental validations independently.

(2) Figure 3: Panels d and e show the same thing. Why would you expect that xz and yz profiles should be different? Is this due to the orientation of the objectives towards the sample?

In Figure 3, we present the PSF from all three orthogonal views, as this provides the most transparent assessment of PSF quality—certain aberration modes can be obscured when only select perspectives are shown. In principle, the XZ and YZ projections should be equivalent in a well-aligned system. However, as seen in the XZ projection, a small degree of coma is present that is not evident in the YZ view. We now explicitly note this observation in the revised figure caption to clarify the difference between these panels.

(3) Figure 4's single boxes lack a scale bar, and some of the Supplementary Figures (e.g. Figure 5) lack detailed axis labels or scale bars. Also, in the detailed documentation, some figures are referred to as Figure 5. Figure 7 or, for example, figure 6. Figure 8, and this makes the cross-references very complicated to follow

In the revised manuscript, we have corrected these issues. All figures and supplementary figures now include appropriate scale bars, axis labels, and consistent formatting. We have also carefully reviewed and standardized all cross-references throughout the main text and supplementary documentation to ensure that figure numbering is accurate and easy to follow.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Zhou and colleagues developed a computational model of replay that heavily builds on cognitive models of memory in context (e.g., the context-maintenance and retrieval model), which have been successfully used to explain memory phenomena in the past. Their model produces results that mirror previous empirical findings in rodents and offers a new computational framework for thinking about replay.

Strengths:

The model is compelling and seems to explain a number of findings from the rodent literature. It is commendable that the authors implement commonly used algorithms from wakefulness to model sleep/rest, thereby linking wake and sleep phenomena in a parsimonious way. Additionally, the manuscript's comprehensive perspective on replay, bridging humans and non-human animals, enhanced its theoretical contribution.

Weaknesses:

This reviewer is not a computational neuroscientist by training, so some comments may stem from misunderstandings. I hope the authors would see those instances as opportunities to clarify their findings for broader audiences.

(1) The model predicts that temporally close items will be co-reactivated, yet evidence from humans suggests that temporal context doesn't guide sleep benefits (instead, semantic connections seem to be of more importance; Liu and Ranganath 2021, Schechtman et al 2023). Could these findings be reconciled with the model or is this a limitation of the current framework?

We appreciate the encouragement to discuss this connection. Our framework can accommodate semantic associations as determinants of sleep-dependent consolidation, which can in principle outweigh temporal associations. Indeed, prior models in this lineage have extensively simulated how semantic associations support encoding and retrieval alongside temporal associations. It would therefore be straightforward to extend our model to simulate how semantic associations guide sleep benefits, and to compare their contribution against that conferred by temporal associations across different experimental paradigms. In the revised manuscript, we have added a discussion of how our framework may simulate the role of semantic associations in sleep-dependent consolidation.

“Several recent studies have argued for dominance of semantic associations over temporal associations in the process of human sleep-dependent consolidation (Schechtman et al., 2023; Liu and Ranganath 2021; Sherman et al., 2025), with one study observing no role at all for temporal associations (Schechtman et al., 2023). At first glance, these findings appear in tension with our model, where temporal associations drive offline consolidation. Indeed, prior models have accounted for these findings by suppressing temporal context during sleep (Liu and Ranganath 2024; Sherman et al., 2025). However, earlier models in the CMR lineage have successfully captured the joint contributions of semantic and temporal associations to encoding and retrieval (Polyn et al., 2009), and these processes could extend naturally to offline replay. In a paradigm where semantic associations are especially salient during awake learning, the model could weight these associations more and account for greater co-reactivation and sleep-dependent memory benefits for semantically related than temporally related items. Consistent with this idea, Schechtman et al. (2023) speculated that their null temporal effects likely reflected the task’s emphasis on semantic associations. When temporal associations are more salient and task-relevant, sleep-related benefits for temporally contiguous items are more likely to emerge (e.g., Drosopoulos et al., 2007; King et al., 2017).”

The reviewer’s comment points to fruitful directions for future work that could employ our framework to dissect the relative contributions of semantic and temporal associations to memory consolidation.

(2) During replay, the model is set so that the next reactivated item is sampled without replacement (i.e., the model cannot get "stuck" on a single item). I'm not sure what the biological backing behind this is and why the brain can't reactivate the same item consistently.

Furthermore, I'm afraid that such a rule may artificially generate sequential reactivation of items regardless of wake training. Could the authors explain this better or show that this isn't the case?

We appreciate the opportunity to clarify this aspect of the model. We first note that this mechanism has long been a fundamental component of this class of models (Howard & Kahana 2002). Many classic memory models (Brown et al., 2000; Burgess & Hitch, 1991; Lewandowsky & Murdock 1989) incorporate response suppression, in which activated items are temporarily inhibited. The simplest implementation, which we use here, removes activated items from the pool of candidate items. Alternative implementations achieve this through transient inhibition, often conceptualized as neuronal fatigue (Burgess & Hitch, 1991; Grossberg 1978). Our model adopts a similar perspective, interpreting this mechanism as mimicking a brief refractory period that renders reactivated neurons unlikely to fire again within a short physiological event such as a sharp-wave ripple. Importantly, this approach does not generate spurious sequences. Instead, the model’s ability to preserve the structure of wake experience during replay depends entirely on the learned associations between items (without these associations, item order would be random). Similar assumptions are also common in models of replay. For example, reinforcement learning models of replay incorporate mechanisms such as inhibition to prevent repeated reactivations (e.g., Diekmann & Cheng, 2023) or prioritize reactivation based on ranking to limit items to a single replay (e.g., Mattar & Daw, 2018). We now discuss these points in the section titled “A context model of memory replay”

“This mechanism of sampling without replacement, akin to response suppression in established context memory models (Howard & Kahana 2002), could be implemented by neuronal fatigue or refractory dynamics (Burgess & Hitch, 1991; Grossberg 1978). Non-repetition during reactivation is also a common assumption in replay models that regulate reactivation through inhibition or prioritization (Diekmann & Cheng 2023; Mattar & Daw 2018; Singh et al., 2022).”

(3) If I understand correctly, there are two ways in which novelty (i.e., less exposure) is accounted for in the model. The first and more talked about is the suppression mechanism (lines 639-646). The second is a change in learning rates (lines 593-595). It's unclear to me why both procedures are needed, how they differ, and whether these are two different mechanisms that the model implements. Also, since the authors controlled the extent to which each item was experienced during wakefulness, it's not entirely clear to me which of the simulations manipulated novelty on an individual item level, as described in lines 593-595 (if any).

We agree that these mechanisms and their relationships would benefit from clarification. As noted, novelty influences learning through two distinct mechanisms. First, the suppression mechanism is essential for capturing the inverse relationship between the amount of wake experience and the frequency of replay, as observed in several studies. This mechanism ensures that items with high wake activity are less likely to dominate replay. Second, the decrease in learning rates with repetition is crucial for preserving the stochasticity of replay. Without this mechanism, the model would increase weights linearly, leading to an exponential increase in the probability of successive wake items being reactivated back-to-back due to the use of a softmax choice rule. This would result in deterministic replay patterns, which are inconsistent with experimental observations.

We have revised the Methods section to explicitly distinguish these two mechanisms:

“This experience-dependent suppression mechanism is distinct from the reduction of learning rates through repetition; it does not modulate the update of memory associations but exclusively governs which items are most likely to initiate replay.”

We have also clarified our rationale for including a learning rate reduction mechanism:

“The reduction in learning rates with repetition is important for maintaining a degree of stochasticity in the model’s replay during task repetition, since linearly increasing weights would, through the softmax choice rule, exponentially amplify differences in item reactivation probabilities, sharply reducing variability in replay.”

Finally, we now specify exactly where the learning-rate reduction applied, namely in simulations where sequences are repeated across multiple sessions:

“In this simulation, the learning rates progressively decrease across sessions, as described above.“

As to the first mechanism - experience-based suppression - I find it challenging to think of a biological mechanism that would achieve this and is selectively activated immediately before sleep (somehow anticipating its onset). In fact, the prominent synaptic homeostasis hypothesis suggests that such suppression, at least on a synaptic level, is exactly what sleep itself does (i.e., prune or weaken synapses that were enhanced due to learning during the day). This begs the question of whether certain sleep stages (or ultradian cycles) may be involved in pruning, whereas others leverage its results for reactivation (e.g., a sequential hypothesis; Rasch & Born, 2013). That could be a compelling synthesis of this literature. Regardless of whether the authors agree, I believe that this point is a major caveat to the current model. It is addressed in the discussion, but perhaps it would be beneficial to explicitly state to what extent the results rely on the assumption of a pre-sleep suppression mechanism.

We appreciate the reviewer raising this important point. Unlike the mechanism proposed by the synaptic homeostasis hypothesis, the suppression mechanism in our model does not suppress items based on synapse strength, nor does it modify synaptic weights. Instead, it determines the level of suppression for each item based on activity during awake experience. The brain could implement such a mechanism by tagging each item according to its activity level during wakefulness. During subsequent consolidation, the initial reactivation of an item during replay would reflect this tag, influencing how easily it can be reactivated.

A related hypothesis has been proposed in recent work, suggesting that replay avoids recently active trajectories due to spike frequency adaptation in neurons (Mallory et al., 2024). Similarly, the suppression mechanism in our model is critical for explaining the observed negative relationship between the amount of recent wake experience and the degree of replay.

We discuss the biological plausibility of this mechanism and its relationship with existing models in the Introduction. In the section titled “The influence of experience”, we have added the following:

“Our model implements an activity‑dependent suppression mechanism that, at the onset of each offline replay event, assigns each item a selection probability inversely proportional to its activation during preceding wakefulness. The brain could implement this by tagging each memory trace in proportion to its recent activation; during consolidation, that tag would then regulate starting replay probability, making highly active items less likely to be reactivated. A recent paper found that replay avoids recently traversed trajectories through awake spike‑frequency adaptation (Mallory et al., 2025), which could implement this kind of mechanism. In our simulations, this suppression is essential for capturing the inverse relationship between replay frequency and prior experience. Note that, unlike the synaptic homeostasis hypothesis (Tononi & Cirelli 2006), which proposes that the brain globally downscales synaptic weights during sleep, this mechanism leaves synaptic weights unchanged and instead biases the selection process during replay.”

(4) As the manuscript mentions, the only difference between sleep and wake in the model is the initial conditions (a0). This is an obvious simplification, especially given the last author's recent models discussing the very different roles of REM vs NREM. Could the authors suggest how different sleep stages may relate to the model or how it could be developed to interact with other successful models such as the ones the last author has developed (e.g., C-HORSE)? 

We appreciate the encouragement to comment on the roles of different sleep stages in the manuscript, especially since, as noted, the lab is very interested in this and has explored it in other work. We chose to focus on NREM in this work because the vast majority of electrophysiological studies of sleep replay have identified these events during NREM. In addition, our lab’s theory of the role of REM (Singh et al., 2022, PNAS) is that it is a time for the neocortex to replay remote memories, in complement to the more recent memories replayed during NREM. The experiments we simulate all involve recent memories. Indeed, our view is that part of the reason that there is so little data on REM replay may be that experimenters are almost always looking for traces of recent memories (for good practical and technical reasons).

Regarding the simplicity of the distinction between simulated wake and sleep replay, we view it as an asset of the model that it can account for many of the different characteristics of awake and NREM replay with very simple assumptions about differences in the initial conditions. There are of course many other differences between the states that could be relevant to the impact of replay, but the current target empirical data did not necessitate us taking those into account. This allows us to argue that differences in initial conditions should play a substantial role in an account of the differences between wake and sleep replay.

We have added discussion of these ideas and how they might be incorporated into future versions of the model in the Discussion section:

“Our current simulations have focused on NREM, since the vast majority of electrophysiological studies of sleep replay have identified replay events in this stage. We have proposed in other work that replay during REM sleep may provide a complementary role to NREM sleep, allowing neocortical areas to reinstate remote, already-consolidated memories that need to be integrated with the memories that were recently encoded in the hippocampus and replayed during NREM (Singh et al., 2022). An extension of our model could undertake this kind of continual learning setup, where the student but not teacher network retains remote memories, and the driver of replay alternates between hippocampus (NREM) and cortex (REM) over the course of a night of simulated sleep. Other differences between stages of sleep and between sleep and wake states are likely to become important for a full account of how replay impacts memory. Our current model parsimoniously explains a range of differences between awake and sleep replay by assuming simple differences in initial conditions, but we expect many more characteristics of these states (e.g., neural activity levels, oscillatory profiles, neurotransmitter levels, etc.) will be useful to incorporate in the future.”

Finally, I wonder how the model would explain findings (including the authors') showing a preference for reactivation of weaker memories. The literature seems to suggest that it isn't just a matter of novelty or exposure, but encoding strength. Can the model explain this? Or would it require additional assumptions or some mechanism for selective endogenous reactivation during sleep and rest?

We appreciate the encouragement to discuss this, as we do think the model could explain findings showing a preference for reactivation of weaker memories, as in Schapiro et al. (2018). In our framework, memory strength is reflected in the magnitude of each memory’s associated synaptic weights, so that stronger memories yield higher retrieved‑context activity during wake encoding than weaker ones. Because the model’s suppression mechanism reduces an item’s replay probability in proportion to its retrieved‑context activity, items with larger weights (strong memories) are more heavily suppressed at the onset of replay, while those with smaller weights (weaker memories) receive less suppression. When items have matched reward exposure, this dynamic would bias offline replay toward weaker memories, therefore preferentially reactivating weak memories. 

In the section titled “The influence of experience”, we updated a sentence to discuss this idea more explicitly: 

“Such a suppression mechanism may be adaptive, allowing replay to benefit not only the most recently or strongly encoded items but also to provide opportunities for the consolidation of weaker or older memories, consistent with empirical evidence (e.g., Schapiro et al. 2018; Yu et al., 2024).”

(5) Lines 186-200 - Perhaps I'm misunderstanding, but wouldn't it be trivial that an external cue at the end-item of Figure 7a would result in backward replay, simply because there is no potential for forward replay for sequences starting at the last item (there simply aren't any subsequent items)? The opposite is true, of course, for the first-item replay, which can't go backward. More generally, my understanding of the literature on forward vs backward replay is that neither is linked to the rodent's location. Both commonly happen at a resting station that is further away from the track. It seems as though the model's result may not hold if replay occurs away from the track (i.e. if a0 would be equal for both pre- and post-run).

In studies where animals run back and forth on a linear track, replay events are decoded separately for left and right runs, identifying both forward and reverse sequences for each direction, for example using direction-specific place cell sequence templates. Accordingly, in our simulation of, e.g., Ambrose et al. (2016), we use two independent sequences, one for left runs and one for right runs (an approach that has been taken in prior replay modeling work). Crucially, our model assumes a context reset between running episodes, preventing the final item of one traversal from acquiring contextual associations with the first item of the next. As a result, learning in the two sequences remains independent, and when an external cue is presented at the track’s end, replay predominantly unfolds in the backward direction, only occasionally producing forward segments when the cue briefly reactivates an earlier sequence item before proceeding forward.

We added a note to the section titled “The context-dependency of memory replay” to clarify this:

“In our model, these patterns are identical to those in our simulation of Ambrose et al. (2016), which uses two independent sequences to mimic the two run directions. This is because the drifting context resets before each run sequence is encoded, with the pause between runs acting as an event boundary that prevents the final item of one traversal from associating with the first item of the next, thereby keeping learning in each direction independent.”

To our knowledge, no study has observed a similar asymmetry when animals are fully removed from the track, although both types of replay can be observed when animals are away from the track. For example, Gupta et al. (2010) demonstrated that when animals replay trajectories far from their current location, the ratio of forward vs. backward replay appears more balanced. We now highlight this result in the manuscript and explain how it aligns with the predictions of our model:

“For example, in tasks where the goal is positioned in the middle of an arm rather than at its end, CMR-replay predicts a more balanced ratio of forward and reverse replay, whereas the EVB model still predicts a dominance of reverse replay due to backward gain propagation from the reward. This contrast aligns with empirical findings showing that when the goal is located in the middle of an arm, replay events are more evenly split between forward and reverse directions (Gupta et al., 2010), whereas placing the goal at the end of a track produces a stronger bias toward reverse replay (Diba & Buzsaki 2007).” 

Although no studies, to our knowledge, have observed a context-dependent asymmetry between forward and backward replay when the animal is away from the track, our model does posit conditions under which it could. Specifically, it predicts that deliberation on a specific memory, such as during planning, could generate an internal context input that biases replay: actively recalling the first item of a sequence may favor forward replay, while thinking about the last item may promote backward replay, even when the individual is physically distant from the track.

We now discuss this prediction in the section titled “The context-dependency of memory replay”:

“Our model also predicts that deliberation on a specific memory, such as during planning, could serve to elicit an internal context cue that biases replay: actively recalling the first item of a sequence may favor forward replay, while thinking about the last item may promote backward replay, even when the individual is physically distant from the track. While not explored here, this mechanism presents a potential avenue for future modeling and empirical work.”

(6) The manuscript describes a study by Bendor & Wilson (2012) and tightly mimics their results. However, notably, that study did not find triggered replay immediately following sound presentation, but rather a general bias toward reactivation of the cued sequence over longer stretches of time. In other words, it seems that the model's results don't fully mirror the empirical results. One idea that came to mind is that perhaps it is the R/L context - not the first R/L item - that is cued in this study. This is in line with other TMR studies showing what may be seen as contextual reactivation. If the authors think that such a simulation may better mirror the empirical results, I encourage them to try. If not, however, this limitation should be discussed.

Although our model predicts that replay is triggered immediately by the sound cue, it also predicts a sustained bias toward the cued sequence. Replay in our model unfolds across the rest phase as multiple successive events, so the bias observed in our sleep simulations indeed reflects a prolonged preference for the cued sequence.

We now discuss this issue, acknowledging the discrepancy:

“Bendor and Wilson (2012) found that sound cues during sleep did not trigger immediate replay, but instead biased reactivation toward the cued sequence over an extended period of time. While the model does exhibit some replay triggered immediately by the cue, it also captures the sustained bias toward the cued sequence over an extended period.”

Second, within this framework, context is modeled as a weighted average of the features associated with items. As a result, cueing the model with the first R/L item produces qualitatively similar outcomes as cueing it with a more extended R/L cue that incorporates features of additional items. This is because both approaches ultimately use context features unique to the two sides.

(7) There is some discussion about replay's benefit to memory. One point of interest could be whether this benefit changes between wake and sleep. Relatedly, it would be interesting to see whether the proportion of forward replay, backward replay, or both correlated with memory benefits. I encourage the authors to extend the section on the function of replay and explore these questions.

We thank the reviewer for this suggestion. Regarding differences in the contribution of wake and sleep to memory, our current simulations predict that compared to rest in the task environment, sleep is less biased toward initiating replay at specific items, leading to a more uniform benefit across all memories. Regarding the contributions of forward and backward replay, our model predicts that both strengthen bidirectional associations between items and contexts, benefiting memory in qualitatively similar ways. Furthermore, we suggest that the offline learning captured  by our teacher-student simulations reflects consolidation processes that are specific to sleep.

We have expanded the section titled “The influence of experience” to discuss these predictions of the model: 

“The results outlined above arise from the model's assumption that replay strengthens bidirectional associations between items and contexts to benefit memory. This assumption leads to several predictions about differences across replay types. First, the model predicts that sleep yields different memory benefits compared to rest in the task environment: Sleep is less biased toward initiating replay at specific items, resulting in a more uniform benefit across all memories. Second, the model predicts that forward and backward replay contribute to memory in qualitatively similar ways but tend to benefit different memories. This divergence arises because forward and backward replay exhibit distinct item preferences, with backward replay being more likely to include rewarded items, thereby preferentially benefiting those memories.”

We also updated the “The function of replay” section to include our teacher-student speculation:

“We speculate that the offline learning observed in these simulations corresponds to consolidation processes that operate specifically during sleep, when hippocampal-neocortical dynamics are especially tightly coupled (Klinzing et al., 2019).”

(8) Replay has been mostly studied in rodents, with few exceptions, whereas CMR and similar models have mostly been used in humans. Although replay is considered a good model of episodic memory, it is still limited due to limited findings of sequential replay in humans and its reliance on very structured and inherently autocorrelated items (i.e., place fields). I'm wondering if the authors could speak to the implications of those limitations on the generalizability of their model. Relatedly, I wonder if the model could or does lead to generalization to some extent in a way that would align with the complementary learning systems framework.

We appreciate these insightful comments. Traditionally, replay studies have focused on spatial tasks with autocorrelated item representations (e.g., place fields). However, an increasing number of human studies have demonstrated sequential replay using stimuli with distinct, unrelated representations. Our model is designed to accommodate both scenarios. In our current simulations, we employ orthogonal item representations while leveraging a shared, temporally autocorrelated context to link successive items. We anticipate that incorporating autocorrelated item representations would further enhance sequence memory by increasing the similarity between successive contexts. Overall, we believe that the model generalizes across a broad range of experimental settings, regardless of the degree of autocorrelation between items. Moreover, the underlying framework has been successfully applied to explain sequential memory in both spatial domains, explaining place cell firing properties (e.g., Howard et al., 2004), and in non-spatial domains, such as free recall experiments where items are arbitrarily related. 

In the section titled “A context model of memory replay”, we added this comment to address this point:

“Its contiguity bias stems from its use of shared, temporally autocorrelated context to link successive items, despite the orthogonal nature of individual item representations. This bias would be even stronger if items had overlapping representations, as observed in place fields.”

Since CMR-replay learns distributed context representations where overlap across context vectors captures associative structure, and replay helps strengthen that overlap, this could indeed be viewed as consonant with complementary learning systems integration processes. 

Reviewer #2 (Public Review):

This manuscript proposes a model of replay that focuses on the relation between an item and its context, without considering the value of the item. The model simulates awake learning, awake replay, and sleep replay, and demonstrates parallels between memory phenomenon driven by encoding strength, replay of sequence learning, and activation of nearest neighbor to infer causality. There is some discussion of the importance of suppression/inhibition to reduce activation of only dominant memories to be replayed, potentially boosting memories that are weakly encoded. Very nice replications of several key replay findings including the effect of reward and remote replay, demonstrating the equally salient cue of context for offline memory consolidation.

I have no suggestions for the main body of the study, including methods and simulations, as the work is comprehensive, transparent, and well-described. However, I would like to understand how the CMRreplay model fits with the current understanding of the importance of excitation vs inhibition, remembering vs forgetting, activation vs deactivation, strengthening vs elimination of synapses, and even NREM vs REM as Schapiro has modeled. There seems to be a strong association with the efforts of the model to instantiate a memory as well as how that reinstantiation changes across time. But that is not all this is to consolidation. The specific roles of different brain states and how they might change replay is also an important consideration.

We are gratified that the reviewer appreciated the work, and we agree that the paper would benefit from comment on the connections to these other features of consolidation.

Excitation vs. inhibition: CMR-replay does not model variations in the excitation-inhibition balance across brain states (as in other models, e.g., Chenkov et al., 2017), since it does not include inhibitory connections. However, we posit that the experience-dependent suppression mechanism in the model might, in the brain, involve inhibitory processes. Supporting this idea, studies have observed increased inhibition with task repetition (Berners-Lee et al., 2022). We hypothesize that such mechanisms may underlie the observed inverse relationship between task experience and replay frequency in many studies. We discuss this in the section titled “A context model of memory replay”:

“The proposal that a suppression mechanism plays a role in replay aligns with models that regulate place cell reactivation via inhibition (Malerba et al., 2016) and with empirical observations of increased hippocampal inhibitory interneuron activity with experience (Berners-Lee et al., 2022). Our model assumes the presence of such inhibitory mechanisms but does not explicitly model them.”

Remembering/forgetting, activation/deactivation, and strengthening/elimination of synapses: The model does not simulate synaptic weight reduction or pruning, so it does not forget memories through the weakening of associated weights. However, forgetting can occur when a memory is replayed less frequently than others, leading to reduced activation of that memory compared to its competitors during context-driven retrieval. In the Discussion section, we acknowledge that a biologically implausible aspect of our model is that it implements only synaptic strengthening: 

“Aspects of the model, such as its lack of regulation of the cumulative positive weight changes that can accrue through repeated replay, are biologically implausible (as biological learning results in both increases and decreases in synaptic weights) and limit the ability to engage with certain forms of low level neural data (e.g., changes in spine density over sleep periods; de Vivo et al., 2017; Maret et al., 2011). It will be useful for future work to explore model variants with more elements of biological plausibility.” Different brain states and NREM vs REM: Reviewer 1 also raised this important issue (see above). We have added the following thoughts on differences between these states and the relationship to our prior work to the Discussion section:

“Our current simulations have focused on NREM, since the vast majority of electrophysiological studies of sleep replay have identified replay events in this stage. We have proposed in other work that replay during REM sleep may provide a complementary role to NREM sleep, allowing neocortical areas to reinstate remote, already-consolidated memories that need to be integrated with the memories that were recently encoded in the hippocampus and replayed during NREM (Singh et al., 2022). An extension of our model could undertake this kind of continual learning setup, where the student but not teacher network retains remote memories, and the driver of replay alternates between hippocampus (NREM) and cortex (REM) over the course of a night of simulated sleep. Other differences between stages of sleep and between sleep and wake states are likely to become important for a full account of how replay impacts memory. Our current model parsimoniously explains a range of differences between awake and sleep replay by assuming simple differences in initial conditions, but we expect many more characteristics of these states (e.g., neural activity levels, oscillatory profiles, neurotransmitter levels, etc.) will be useful to incorporate in the future.”

We hope these points clarify the model’s scope and its potential for future extensions.

Do the authors suggest that these replay systems are more universal to offline processes beyond episodic memory? What about procedural memories and working memory?

We thank the reviewer for raising this important question. We have clarified in the manuscript:

“We focus on the model as a formulation of hippocampal replay, capturing how the hippocampus may replay past experiences through simple and interpretable mechanisms.”

With respect to other forms of memory, we now note that:

“This motor memory simulation using a model of hippocampal replay is consistent with evidence that hippocampal replay can contribute to consolidating memories that are not hippocampally dependent at encoding (Schapiro et al., 2019; Sawangjit et al., 2018). It is possible that replay in other, more domain-specific areas could also contribute (Eichenlaub et al., 2020).”

Though this is not a biophysical model per se, can the authors speak to the neuromodulatory milieus that give rise to the different types of replay?

Our work aligns with the perspective proposed by Hasselmo (1999), which suggests that waking and sleep states differ in the degree to which hippocampal activity is driven by external inputs. Specifically, high acetylcholine levels during waking bias activity to flow into the hippocampus, while low acetylcholine levels during sleep allow hippocampal activity to influence other brain regions. Consistent with this view, our model posits that wake replay is more biased toward items associated with the current resting location due to the presence of external input during waking states. In the Discussion section, we have added a comment on this point:

“Our view aligns with the theory proposed by Hasselmo (1999), which suggests that the degree of hippocampal activity driven by external inputs differs between waking and sleep states: High acetylcholine levels during wakefulness bias activity into the hippocampus, while low acetylcholine levels during slow-wave sleep allow hippocampal activity to influence other brain regions.”

Reviewer #3 (Public Review):

In this manuscript, Zhou et al. present a computational model of memory replay. Their model (CMR-replay) draws from temporal context models of human memory (e.g., TCM, CMR) and claims replay may be another instance of a context-guided memory process. During awake learning, CMR replay (like its predecessors) encodes items alongside a drifting mental context that maintains a recency-weighted history of recently encoded contexts/items. In this way, the presently encoded item becomes associated with other recently learned items via their shared context representation - giving rise to typical effects in recall such as primacy, recency, and contiguity. Unlike its predecessors, CMR-replay has built-in replay periods. These replay periods are designed to approximate sleep or wakeful quiescence, in which an item is spontaneously reactivated, causing a subsequent cascade of item-context reactivations that further update the model's item-context associations.

Using this model of replay, Zhou et al. were able to reproduce a variety of empirical findings in the replay literature: e.g., greater forward replay at the beginning of a track and more backward replay at the end; more replay for rewarded events; the occurrence of remote replay; reduced replay for repeated items, etc. Furthermore, the model diverges considerably (in implementation and predictions) from other prominent models of replay that, instead, emphasize replay as a way of predicting value from a reinforcement learning framing (i.e., EVB, expected value backup).

Overall, I found the manuscript clear and easy to follow, despite not being a computational modeller myself. (Which is pretty commendable, I'd say). The model also was effective at capturing several important empirical results from the replay literature while relying on a concise set of mechanisms - which will have implications for subsequent theory-building in the field.

With respect to weaknesses, additional details for some of the methods and results would help the readers better evaluate the data presented here (e.g., explicitly defining how the various 'proportion of replay' DVs were calculated).

For example, for many of the simulations, the y-axis scale differs from the empirical data despite using comparable units, like the proportion of replay events (e.g., Figures 1B and C). Presumably, this was done to emphasize the similarity between the empirical and model data. But, as a reader, I often found myself doing the mental manipulation myself anyway to better evaluate how the model compared to the empirical data. Please consider using comparable y-axis ranges across empirical and simulated data wherever possible.

We appreciate this point. As in many replay modeling studies, our primary goal is to provide a qualitative fit that demonstrates the general direction of differences between our model and empirical data, without engaging in detailed parameter fitting for a precise quantitative fit. Still, we agree that where possible, it is useful to better match the axes. We have updated figures 2B and 2C so that the y-axis scales are more directly comparable between the empirical and simulated data. 

In a similar vein to the above point, while the DVs in the simulations/empirical data made intuitive sense, I wasn't always sure precisely how they were calculated. Consider the "proportion of replay" in Figure 1A. In the Methods (perhaps under Task Simulations), it should specify exactly how this proportion was calculated (e.g., proportions of all replay events, both forwards and backwards, combining across all simulations from Pre- and Post-run rest periods). In many of the examples, the proportions seem to possibly sum to 1 (e.g., Figure 1A), but in other cases, this doesn't seem to be true (e.g., Figure 3A). More clarity here is critical to help readers evaluate these data. Furthermore, sometimes the labels themselves are not the most informative. For example, in Figure 1A, the y-axis is "Proportion of replay" and in 1C it is the "Proportion of events". I presumed those were the same thing - the proportion of replay events - but it would be best if the axis labels were consistent across figures in this manuscript when they reflect the same DV.

We appreciate these useful suggestions. We have revised the Methods section to explain in detail how DVs are calculated for each simulation. The revisions clarify the differences between related measures, such as those shown in Figures 1A and 1C, so that readers can more easily see how the DVs are defined and interpreted in each case. 

Reviewer #4/Reviewing Editor (Public Review):

Summary:

With their 'CMR-replay' model, Zhou et al. demonstrate that the use of spontaneous neural cascades in a context-maintenance and retrieval (CMR) model significantly expands the range of captured memory phenomena.

Strengths:

The proposed model compellingly outperforms its CMR predecessor and, thus, makes important strides towards understanding the empirical memory literature, as well as highlighting a cognitive function of replay.

Weaknesses:

Competing accounts of replay are acknowledged but there are no formal comparisons and only CMR-replay predictions are visualized. Indeed, other than the CMR model, only one alternative account is given serious consideration: A variant of the 'Dyna-replay' architecture, originally developed in the machine learning literature (Sutton, 1990; Moore & Atkeson, 1993) and modified by Mattar et al (2018) such that previously experienced event-sequences get replayed based on their relevance to future gain. Mattar et al acknowledged that a realistic Dyna-replay mechanism would require a learned representation of transitions between perceptual and motor events, i.e., a 'cognitive map'. While Zhou et al. note that the CMR-replay model might provide such a complementary mechanism, they emphasize that their account captures replay characteristics that Dyna-replay does not (though it is unclear to what extent the reverse is also true).

We thank the reviewer for these thoughtful comments and appreciate the opportunity to clarify our approach. Our goal in this work is to contrast two dominant perspectives in replay research: replay as a mechanism for learning reward predictions and replay as a process for memory consolidation. These models were chosen as representatives of their classes of models because they use simple and interpretable mechanisms that can simulate a wide range of replay phenomena, making them ideal for contrasting these two perspectives.

Although we implemented CMR-replay as a straightforward example of the memory-focused view, we believe the proposed mechanisms could be extended to other architectures, such as recurrent neural networks, to produce similar results. We now discuss this possibility in the revised manuscript (see below). However, given our primary goal of providing a broad and qualitative contrast of these two broad perspectives, we decided not to undertake simulations with additional individual models for this paper.

Regarding the Mattar & Daw model, it is true that a mechanistic implementation would require a mechanism that avoids precomputing priorities before replay. However, the "need" component of their model already incorporates learned expectations of transitions between actions and events. Thus, the model's limitations are not due to the absence of a cognitive map.

In contrast, while CMR-replay also accumulates memory associations that reflect experienced transitions among events, it generates several qualitatively distinct predictions compared to the Mattar & Daw model. As we note in the manuscript, these distinctions make CMR-replay a contrasting rather than complementary perspective.

Another important consideration, however, is how CMR replay compares to alternative mechanistic accounts of cognitive maps. For example, Recurrent Neural Networks are adept at detecting spatial and temporal dependencies in sequential input; these networks are being increasingly used to capture psychological and neuroscientific data (e.g., Zhang et al, 2020; Spoerer et al, 2020), including hippocampal replay specifically (Haga & Fukai, 2018). Another relevant framework is provided by Associative Learning Theory, in which bidirectional associations between static and transient stimulus elements are commonly used to explain contextual and cue-based phenomena, including associative retrieval of absent events (McLaren et al, 1989; Harris, 2006; Kokkola et al, 2019). Without proper integration with these modeling approaches, it is difficult to gauge the innovation and significance of CMR-replay, particularly since the model is applied post hoc to the relatively narrow domain of rodent maze navigation.

First, we would like to clarify our principal aim in this work is to characterize the nature of replay, rather than to model cognitive maps per se. Accordingly, CMR‑replay is not designed to simulate head‐direction signals, perform path integration, or explain the spatial firing properties of neurons during navigation. Instead, it focuses squarely on sequential replay phenomena, simulating classic rodent maze reactivation studies and human sequence‐learning tasks. These simulations span a broad array of replay experimental paradigms to ensure extensive coverage of the replay findings reported across the literature. As such, the contribution of this work is in explaining the mechanisms and functional roles of replay, and demonstrating that a model that employs simple and interpretable memory mechanisms not only explains replay phenomena traditionally interpreted through a value-based lens but also accounts for findings not addressed by other memory-focused models.

As the reviewer notes, CMR-replay shares features with other memory-focused models. However, to our knowledge, none of these related approaches have yet captured the full suite of empirical replay phenomena, suggesting the combination of mechanisms employed in CMR-replay is essential for explaining these phenomena. In the Discussion section, we now discuss the similarities between CMR-replay and related memory models and the possibility of integrating these approaches:

“Our theory builds on a lineage of memory-focused models, demonstrating the power of this perspective in explaining phenomena that have often been attributed to the optimization of value-based predictions. In this work, we focus on CMR-replay, which exemplifies the memory-centric approach through a set of simple and interpretable mechanisms that we believe are broadly applicable across memory domains. Elements of CMR-replay share similarities with other models that adopt a memory-focused perspective. The model learns distributed context representations whose overlaps encodes associations among items, echoing associative learning theories in which overlapping patterns capture stimulus similarity and learned associations (McLaren & Mackintosh 2002). Context evolves through bidirectional interactions between items and their contextual representations, mirroring the dynamics found in recurrent neural networks (Haga & Futai 2018; Levenstein et al., 2024). However, these related approaches have not been shown to account for the present set of replay findings and lack mechanisms—such as reward-modulated encoding and experience-dependent suppression—that our simulations suggest are essential for capturing these phenomena. While not explored here, we believe these mechanisms could be integrated into architectures like recurrent neural networks (Levenstein et al., 2024) to support a broader range of replay dynamics.”

Recommendations For The Authors

Reviewer #1 (Recommendations For The Authors):

(1) Lines 94-96: These lines may be better positioned earlier in the paragraph.

We now introduce these lines earlier in the paragraph.

(2) Line 103 - It's unclear to me what is meant by the statement that "the current context contains contexts associated with previous items". I understand why a slowly drifting context will coincide and therefore link with multiple items that progress rapidly in time, so multiple items will be linked to the same context and each item will be linked to multiple contexts. Is that the idea conveyed here or am I missing something? I'm similarly confused by line 129, which mentions that a context is updated by incorporating other items' contexts. How could a context contain other contexts?

In the model, each item has an associated context that can be retrieved via Mfc. This is true even before learning, since Mfc is initialized as an identity matrix. During learning and replay, we have a drifting context c that is updated each time an item is presented. At each timestep, the model first retrieves the current item’s associated context cf by Mfc, and incorporates it into c. Equation #2 in the Methods section illustrates this procedure in detail. Because of this procedure, the drifting context c is a weighted sum of past items’ associated contexts. 

We recognize that these descriptions can be confusing. We have updated the Results section to better distinguish the drifting context from items’ associated context. For example, we note that:

“We represent the drifting context during learning and replay with c and an item's associated context with cf.”

We have also updated our description of the context drift procedure to distinguish these two quantities: 

“During awake encoding of a sequence of items, for each item f, the model retrieves its associated context cf via Mfc. The drifting context c incorporates the item's associated context cf and downweights its representation of previous items' associated contexts (Figure 1c). Thus, the context layer maintains a recency weighted sum of past and present items' associated contexts.”

(3) Figure 1b and 1d - please clarify which axis in the association matrices represents the item and the context.

We have added labels to show what the axes represent in Figure 1.

(4) The terms "experience" and "item" are used interchangeably and it may be best to stick to one term.

We now use the term “item” wherever we describe the model results. 

(5) The manuscript describes Figure 6 ahead of earlier figures - the authors may want to reorder their figures to improve readability.

We appreciate this suggestion. We decided to keep the current figure organization since it allows us to group results into different themes and avoid redundancy. 

(6) Lines 662-664 are repeated with a different ending, this is likely an error.

We have fixed this error.

Reviewer #3 (Recommendations For The Authors):

Below, I have outlined some additional points that came to mind in reviewing the manuscript - in no particular order.

(1) Figure 1: I found the ordering of panels a bit confusing in this figure, as the reading direction changes a couple of times in going from A to F. Would perhaps putting panel C in the bottom left corner and then D at the top right, with E and F below (also on the right) work?

We agree that this improves the figure. We have restructured the ordering of panels in this figure. 

(2) Simulation 1: When reading the intro/results for the first simulation (Figure 2a; Diba & Buszaki, 2007; "When animals traverse a linear track...", page 6, line 186). It wasn't clear to me why pre-run rest would have any forward replay, particularly if pre-run implied that the animal had no experience with the track yet. But in the Methods this becomes clearer, as the model encodes the track eight times prior to the rest periods. Making this explicit in the text would make it easier to follow. Also, was there any reason why specifically eight sessions of awake learning, in particular, were used?

We now make more explicit that the animals have experience with the track before pre-run rest recording:

“Animals first acquire experience with a linear track by traversing it to collect a reward. Then, during the pre-run rest recording, forward replay predominates.”

We included eight sessions of awake learning to match with the number of sessions in Shin et al. (2017), since this simulation attempts to explain data from that study. After each repetition, the model engages in rest. We have revised the Methods section to indicate the motivation for this choice: 

“In the simulation that examines context-dependent forward and backward replay through experience (Figs. 2a and 5a), CMR-replay encodes an input sequence shown in Fig. 7a, which simulates a linear track run with no ambiguity in the direction of inputs, over eight awake learning sessions (as in Shin et al. 2019)”

(3) Frequency of remote replay events: In the simulation based on Gupta et al, how frequently overall does remote replay occur? In the main text, the authors mention the mean frequency with which shortcut replay occurs (i.e., the mean proportion of replay events that contain a shortcut sequence = 0.0046), which was helpful. But, it also made me wonder about the likelihood of remote replay events. I would imagine that remote replay events are infrequent as well - given that it is considerably more likely to replay sequences from the local track, given the recency-weighted mental context. Reporting the above mean proportion for remote and local replay events would be helpful context for the reader.

In Figure 4c, we report the proportion of remote replay in the two experimental conditions of Gupta et al. that we simulate. 

(4) Point of clarification re: backwards replay: Is backwards replay less likely to occur than forward replay overall because of the forward asymmetry associated with these models? For example, for a backwards replay event to occur, the context would need to drift backwards at least five times in a row, in spite of a higher probability of moving one step forward at each of those steps. Am I getting that right?

The reviewer’s interpretation is correct: CMR-replay is more likely to produce forward than backward replay in sleep because of its forward asymmetry. We note that this forward asymmetry leads to high likelihood of forward replay in the section titled “The context-dependency of memory replay”: 

“As with prior retrieved context models (Howard & Kahana 2002; Polyn et al., 2009), CMR-replay encodes stronger forward than backward associations. This asymmetry exists because, during the first encoding of a sequence, an item's associated context contributes only to its ensuing items' encoding contexts. Therefore, after encoding, bringing back an item's associated context is more likely to reactivate its ensuing than preceding items, leading to forward asymmetric replay (Fig. 6d left).”

(5) On terminating a replay period: "At any t, the replay period ends with a probability of 0.1 or if a task-irrelevant item is reactivated." (Figure 1 caption; see also pg 18, line 635). How was the 0.1 decided upon? Also, could you please add some detail as to what a 'task-irrelevant item' would be? From what I understood, the model only learns sequences that represent the points in a track - wouldn't all the points in the track be task-relevant?

This value was arbitrarily chosen as a small value that allows probabilistic stopping. It was not motivated by prior modeling or a systematic search. We have added: “At each timestep, the replay period ends either with a stop probability of 0.1 or if a task-irrelevant item becomes reactivated. (The choice of the value 0.1 was arbitrary; future work could explore the implications of varying this parameter).” 

In addition, we now explain in the paper that task irrelevant items “do not appear as inputs during awake encoding, but compete with task-relevant items for reactivation during replay, simulating the idea that other experiences likely compete with current experiences during periods of retrieval and reactivation.”

(6) Minor typos:

Turn all instances of "nonlocal" into "non-local", or vice versa

"For rest at the end of a run, cexternal is the context associated with the final item in the sequence. For rest at the end of a run, cexternal is the context associated with the start item." (pg 20, line 663) - I believe this is a typo and that the second sentence should begin with "For rest at the START of a run".

We have updated the manuscript to correct these typos. 

(7) Code availability: I may have missed it, but it doesn't seem like the code is currently available for these simulations. Including the commented code in a public repository (Github, OSF) would be very useful in this case.

We now include a Github link to our simulation code: https://github.com/schapirolab/CMR-replay.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

The manuscript by Raices et al., provides some novel insights into the role and interactions between SPO-11 accessory proteins in C. elegans. The authors propose a model of meiotic DSBs regulation, critical to our understanding of DSB formation and ultimately crossover regulation and accurate chromosome segregation. The work also emphasizes the commonalities and species-specific aspects of DSB regulation. 

Strengths: 

This study capitalizes on the strengths of the C. elegans system to uncover genetic interactions between a lSPO-11 accessory proteins. In combination with physical interactions, the authors synthesize their findings into a model, which will serve as the basis for future work, to determine mechanisms of DSB regulation. 

Weaknesses: 

The methodology, although standard, still lacks some rigor, especially with the IPs. 

Reviewer #2 (Public review): 

Summary: 

Meiotic recombination initiates with the formation of DNA double-strand break (DSB) formation, catalyzed by the conserved topoisomerase-like enzyme Spo11. Spo11 requires accessory factors that are poorly conserved across eukaryotes. Previous genetic studies have identified several proteins required for DSB formation in C. elegans to varying degrees; however, how these proteins interact with each other to recruit the DSB-forming machinery to chromosome axes remains unclear. 

In this study, Raices et al. characterized the biochemical and genetic interactions among proteins that are known to promote DSB formation during C. elegans meiosis. The authors examined pairwise interactions using yeast two-hybrid (Y2H) and co-immunoprecipitation and revealed an interaction between a chromatin-associated protein HIM-17 and a transcription factor XND-1. They further confirmed the previously known interaction between DSB-1 and SPO-11 and showed that DSB-1 also interacts with a nematodespecific HIM-5, which is essential for DSB formation on the X chromosome. They also assessed genetic interactions among these proteins, categorizing them into four epistasis groups by comparing phenotypes in double vs. single mutants. Combining these results, the authors proposed a model of how these proteins interact with chromatin loops and are recruited to chromosome axes, offering insights into the process in C. elegans compared to other organisms. 

Weaknesses: 

This work relies heavily on Y2H, which is notorious for having high rates of false positives and false negatives. Although the interactions between HIM-17 and XND-1 and between DSB-1 and HIM-5 were validated by co-IP, the significance of these interactions was not tested in vivo. Cataloging Y2H and genetic interactions does not yield much more insight. The model proposed in Figure 4 is also highly speculative. 

Reviewer #3 (Public review): 

The goal of this work is to understand the regulation of double-strand break formation during meiosis in C. elegans. The authors have analyzed physical and genetic interactions among a subset of factors that have been previously implicated in DSB formation or the number of timing of DSBs: CEP-1, DSB-1, DSB-2, DSB-3, HIM-5, HIM-17, MRE-11, REC-1, PARG-1, and XND-1. 

The 10 proteins that are analyzed here include a diverse set of factors with different functions, based on prior analyses in many published studies. The term "Spo11 accessory factors" has been used in the meiosis literature to describe proteins that directly promote Spo11 cleavage activity, rather than factors that are important for the expression of meiotic proteins or that influence the genome-wide distribution or timing of DSBs. Based on this definition, the known SPO-11 accessory factors in C. elegans include DSB-1, DSB2, DSB-3, and the MRN complex (at least MRE-11 and RAD-50). These are all homologs of proteins that have been studied biochemically and structurally in other organisms. DSB-1 & DSB-2 are homologs of Rec114, while DSB-3 is a homolog of Mei4. Biochemical and structural studies have shown that Rec114 and Mei4 directly modulate Spo11 activity by recruiting Spo11 to chromatin and promoting its dimerization, which is essential for cleavage. The other factors analyzed in this study affect the timing, distribution, or number of RAD-51 foci, but they likely do so indirectly. As elaborated below, XND-1 and HIM-17 are transcription factors that modulate the expression of other meiotic genes, and their role in DSB formation is parsimoniously explained by this regulatory activity. The roles of HIM-5 and REC-1 remain unclear; the reported localization of HIM-5 to autosomes is consistent with a role in transcription (the autosomes are transcriptionally active in the germline, while the X chromosome is largely silent), but its loss-of-function phenotypes are much more limited than those of HIM-17 and XND-1, so it may play a more direct role in DSB formation. The roles of CEP-1 (a Rad53 homolog) and PARG-1 are also ambiguous, but their homologs in other organisms contribute to DNA repair rather than DSB formation. 

We appreciate the reviewer’s clarification. However, the definition of Spo11 accessory factors varies across the literature. Only Keeney and colleagues define these as proteins that physically associate with and activate Spo11 to catalyze DSB formation (Keeney, Lange & Mohibullah, 2014; Lam & Keeney, 2015). In contrast, other authors have used the term more broadly to refer to proteins that promote or regulate Spo11-dependent DSB formation, without necessarily implying a direct interaction with Spo11 (e.g., Panizza et al., 2011; Robert et al., 2016; Stanzione et al., 2016; Li et al., 2021; Lange et al., 2016). Thus, our usage of the term follows this broader functional definition.

An additional significant limitation of the study, as stated in my initial review, is that much of the analysis here relies on cytological visualization of RAD-51 foci as a proxy for DSBs. RAD-51 associates transiently with DSB sites as they undergo repair and is thus limited in its ability to reveal details about the timing or abundance of DSBs since its loading and removal involve additional steps that may be influenced by the factors being analyzed. 

We agree with the reviewer that counting RAD-51 foci provides only an indirect measure of SPO-11–dependent DSBs, as RAD-51 marks sites of repair rather than the breaks themselves. However, we would like to clarify that our current study does not rely on RAD51 foci quantification for any of the analyses or conclusions presented. None of the figures or datasets in this manuscript are based on RAD-51 cytology. Instead, our conclusions are drawn from genetic interactions, biochemical assays, and protein–protein interaction analyses.

The paper focuses extensively on HIM-5, which was previously shown through genetic and cytological analysis to be important for breaks on the X chromosome. The revised manuscript still claims that "HIM-5 mediates interactions with the different accessory factors sub-groups, providing insights into how components on the DNA loops may interact with the chromosome axis." The weak interactions between HIM-5 and DSB-1/2 detected in the Y2H assay do not convincingly support such a role. The idea that HIM-5 directly promotes break formation is also inconsistent with genetic data showing that him5 mutants lack breaks on the X chromosomes, while HIM-5 has been shown to be is enriched on autosomes. Additionally, as noted in my comment to the authors, the localization data for HIM-5 shown in this paper are discordant with prior studies; this discrepancy should be addressed experimentally. 

We appreciate the reviewer’s concerns regarding the interpretation of HIM-5 function.  The weak Y2H interactions between HIM-5 and DSB-1 are not interpreted as direct biochemical evidence of a strong physical interaction, but rather as a potential point of regulatory connection between these pathways. Importantly, these Y2H data are further supported by co-immunoprecipitation experiments, genetic interactions, and the observed mislocalization of HIM-5 in the absence of DSB-1. Together, these complementary results strengthen our conclusion that HIM-5 functionally associates with DSB-promoting complexes.

Regarding HIM-5 localization, the pattern we observe using both anti-GFP staining of the eaIs4 transgene (Phim-5::him-5::GFP) and anti-HA staining of the HIM-5::HA strain is consistent with that reported by McClendon et al. (2016), who validated the same eaIs4 transgene. Although the pattern difers slightly from Meneely et al. (2012), that used a HIM5 antibody that is no longer functional and that has been discontinued by the commercial source. In this prior study, a weak signal was detected in the mitotic region and late pachytene, but stronger signal was seen in early to mid-pachytene. Our imaging— optimized for low background and stable signal—similarly shows robust HIM-5 localization in early and mid-pachytene, supporting the reliability of our GFP and HA-tagged analyses.

The recent analysis of DSB formation in C. elegans males (Engebrecht et al; PloS Genetics; PMID: 41124211) shows that in absence of him-5 there is a significant reduction of CO designation (measured as COSA-1 foci) on autosomes. This study strongly supports a direct and general role for HIM-5 in crossover formation— on both autosomes and on the hermaphrodite X.

This paper describes REC-1 and HIM-5 as paralogs, based on prior analysis in a paper that included some of the same authors (Chung et al., 2015; DOI 10.1101/gad.266056.115). In my initial review I mentioned that this earlier conclusion was likely incorrect and should not be propagated uncritically here. Since the authors have rebutted this comment rather than amending it, I feel it is important to explain my concerns about the conclusions of previous study. Chung et al. found a small region of potential homology between the C. elegans rec-1 and him-5 genes and also reported that him-5; rec-1 double mutants have more severe defects than either single mutant, indicative of a stronger reduction in DSBs. Based on these observations and an additional argument based on microsynteny, they concluded that these two genes arose through recent duplication and divergence. However, as they noted, genes resembling rec-1 are absent from all other Caenorhabditis species, even those most closely related to C. elegans. The hypothesis that two genes are paralogs that arose through duplication and divergence is thus based on their presence in a single species, in the absence of extensive homology or evidence for conserved molecular function. Further, the hypothesis that gene duplication and divergence has given rise to two paralogs that share no evident structural similarity or common interaction partners in the few million years since C. elegans diverged from its closest known relatives is implausible. In contrast, DSB-1 and DSB-2 are both homologs of Rec114 that clearly arose through duplication and divergence within the Caenorhabditis lineage, but much earlier than the proposed split between REC-1 and HIM-5. Two genes that can be unambiguously identified as dsb-1 and dsb-2 are present in genomes throughout the Elegans supergroup and absent in the Angaria supergroup, placing the duplication event at around 18-30 MYA, yet DSB-1 and DSB-2 share much greater similarity in their amino acid sequence, predicted structure, and function than HIM-5 and REC-1. Further, Raices place HIM-5 and REC-1 in different functional complexes (Figure 3B). 

We respectfully disagree with the reviewer’s characterization of the relationship between HIM-5 and REC-1. Our use of the term “paralog” follows the conclusions of Chung et al. (2015), a peer-reviewed study that provided both sequence and microsynteny evidence supporting this relationship. While we acknowledge that the degree of sequence conservation is limited, the evolutionary scenario proposed by Chung et al. remains the only published framework addressing this question. Further the degree of homology between either HIM-5 or REC-1 and the ancestral locus are similar to that observed for DSB-1 and DSB-2 with REC-114 (Hinman et al., 2021). We therefore retain the use of the term “paralog” in reference to these genes. Importantly, our conclusions regarding their distinct molecular and functional roles are independent of this classification.

The authors acknowledge that HIM-17 is a transcription factor that regulates many meiotic genes. Like HIM-17, XND-1 is cytologically enriched along the autosomes in germline nuclei, suggestive of a role in transcription. The Reinke lab performed ChIP-seq in a strain expressing an XND-1::GFP fusion protein and showed that it binds to promoter regions, many of which overlap with the HIM-17-regulated promoters characterized by the Ahringer lab (doi: 10.1126/sciadv.abo4082). Work from the Yanowitz lab has shown that XND-1 influences the transcription of many other genes involved in meiosis (doi: 10.1534/g3.116.035725) and work from the Colaiacovo lab has shown that XND-1 regulates the expression of CRA-1 (doi: 10.1371/journal.pgen.1005029). Additionally, loss of HIM-17 or XND-1 causes pleiotropic phenotypes, consistent with a broad role in gene regulation. Collectively, these data indicate that XND-1 and HIM-17 are transcription factors that are important for the proper expression of many germline-expressed genes. Thus, as stated above, the roles of HIM-17 and XND-1 in DSB formation, as well as their effects on histone modification, are parsimoniously explained by their regulation of the expression of factors that contribute more directly to DSB formation and chromatin modification. I feel strongly that transcription factors should not be described as "SPO-11 accessory factors." 

The ChIP analysis of XND-1 binding sites (using the XND-1::GFP transgene we provided to the Reinke lab) was performed, and Table S3 in the Ahringer paper suggests it is found at germline promoters, although the analysis is not actually provided. We completely agree that at least a subset of XND-1 functions is explained by its regulation of transcriptional targets (as we previously showed for HIM-5). However, like the MES proteins, a subset of which are also autosomal and impact X chromosome gene expression, XND-1 could also be directly regulating chromatin architecture which could have profound effects on DSB formation.  As stated in our prior comments, precedent for the involvement of a chromatin factor in DSB formation is provided by yeast Spp1. 

Recommendations for the authors: 

Editor comments: 

As you can see, the reviewers have additional comments, and the authors can include revisions to address those points prior to publicizing 'a version of record' (e.g. hatching rate assay mentioned by reviewer #1). This type of study, trying to catalog interactions of many factors, inevitably has loose ends, but in my opinion, it does not reduce the value of the study, as long as statements are not misleading. I suggest that the authors address issues by making changes to the main text. After the next round of adjustments by authors, I feel that it will be ready for a version of record, based on the spirit of the current eLife publication model. 

Reviewer #1 (Recommendations for the authors): 

I still have concerns about the HIM-17 IP and immunoblot probing with XND-1 antibodies. While the newly provided whole extract immunoblot clearly shows a XND-1 specific band that goes away in the mutant extracts, there is additional bands that are recognized - the pattern looks different than in the input in Figure 1B. Additionally, there is still a band of the corresponding size in the IPs from extracts not containing the tagged allele of HIM-17, calling into question whether XND-1 is specifically pulled down. 

The authors did not include the hatching rate as pointed out in the original reviews. In the rebuttal: 

"Great question. I guess we need to do this while back out for review. If anyone has suggestions of what to say here. Clearly we overlooked this point but do have the strain." 

We thank the reviewer for this suggestion. We had intended to include a hatching analysis; however, during the course of this work we discovered that our him-17 stock had acquired an additional linked mutation(s) that altered its phenotype and led to inconsistent results. This strain was used to rederive the him-17; eaIs4 double mutant after our original did not survive freeze/thaw. Given the abnormal behavior observed in this line, we concluded that proceeding with the hatching assays could yield unreliable data. We are currently reestablishing a verified him-17 strain, but in the interest of accuracy and reproducibility, we have restricted our analysis in this manuscript to validated datasets derived from confirmed strains.

Reviewer #2 (Recommendations for the authors): 

The authors have addressed most of the previous concerns and substantially improved the manuscript. The new data demonstrate that HIM-5 localization depends on DSB-1, and together with the Y2H and Co-PI results, strengthen the link between HIM-5 and the DSBforming machinery in C. elegans. The remaining points are outlined below: 

Specific comments: 

The font size of texts and labels in the Figure is very small and is hardly legible. Please enlarge them and make them clearly visible (Fig 1A, 1B, 2A, 2B, 2C, 2D, 2E, 3A, 3B, 3C, 3D, 3F)

Done

Although the authors have addressed the specificity of the XND-1 antibody, it remains unclear whether the boxed band is specific to the him-17::3xHA IP, since the same band appears in the control IP, albeit with lower intensity (Fig 1B). Is the ~100 kDa band in the him-17::3xHA IP a modified form XND-1? While antibody specificity was previously demonstrated by IF using xnd-1 mutants, it would be ideal to confirm this on a western blot as well. 

A Western Blot performed using whole cell extracts and probed with the anti- XND-1 antibody has been provided in the revised version of the manuscript (Fig. S1A). This confirms that the antibody specifically recognizes XND-1 protein. We believe that the ~100 kDa band mentioned by the reviewer is likely to be a non-specific cross reaction band detected by the antibody, since an identical band of the same mW was also detected in xnd-1 null mutants (Fig. S1A).

Regarding the IP negative controls, we are firmly convinced the boxed band to be specific, and the fact that a (very) low intensity band is also found in the negative control should not infringe the validity of the HIM-17-XND-1 specific interaction. There is a constellation of similar examples present across the literature, as it is widely acknowledged amongst biochemists that some proteins may “stick” to the beads due their intrinsic biochemical properties despite usage of highly stringent IP buffers. However, the high level of enrichment detected in the IP (as also underlined by the reviewer) corroborates that XND-1 specifically immunoprecipitates with HIM-17 despite a low, non-specific binding to the HA beads is present. If interaction between XND-1 and HIM-17 was non-specific, we logically would have found the band in the IP and the band in the negative control to be of very similar intensity, which is clearly not the case. 

Although co-IP assays are generally considered not a strictly quantitative assay, we want to emphasize that a comparable amount of nuclear extract was employed in both samples as also evidenced by the inputs, in which it is also possible to see that if anything, slightly less  nuclear extracts were employed in the him-17::3xHA; him-5::GFP::3xFLAG vs. the him5::GFP::3xFLAG negative control, corroborating the above mentioned points.

Lastly, it is crucial to mention that mass spectrometry analyses performed on HIM17::3xHA pulldowns show XND-1 as a highly enriched interacting protein (Blazickova et al.; 2025 Nature Comms.), which strongly supports our co-IP results.

The subheading "HIM-5 is the essential factor for meiotic breaks in the X chromosome" does not accurately represent the work described in the Results or in Figure 1. I disagree with the authors' response to the earlier criticism. The issue is not merely semantic. The data do not demonstrate that HIM-5 is required for DSB formation on the X chromosome - this conclusion can only be inferred. What Figure 1 shows is that XND-1 and HIM-17 interact, and that pie-1p-driven HIM-5 expression can partially rescue meiotic defects of him-17 mutants. This supports the conclusion that him-5 is a target of HIM-17/XND-1 in promoting CO formation on the X chromosome. However, the data provide no direct evidence for the claim stated in the subheading. I strongly encourage authors to revise the subheading to more accurately represent the findings presented in the paper. 

After considering the reviewer’s comments, we have revised the subheading to more accurately describe our findings.

In Fig1C, please fix the typo in the last row - "pie1p::him5-::GFP" to "pie-1p::him- 5::GFP".

Done

In Fig 2C, "p" is missing from the label on the right for Phim-5::him-5::GFP.

Done

In Fig 3I, bring the labels (DSB-1/2/3) at the lower right to the front.

Done

In Concluding Remarks, please fix the typo "frequently".

Done

Reviewer #3 (Recommendations for the authors): 

The experiments that analyze HIM-5 in dsb-1 mutants should be repeated using antibodies against the endogenous HIM-5 antibody, and localization of the HIM-5::HA and HIM-5::GFP proteins should be compared directly to antibody staining. This work uses an epitopetagged protein and a GFP-tagged protein to analyze the localization of HIM-5, while prior work (Meneely et al., 2012) used an antibody against the endogenous protein. In Figures 2 and S4 of this paper, neither HIM-5::HA nor HIM-5::GFP appears to localize strongly to chromatin, and autosomal enrichment of HIM-5, as previously reported for the endogenous protein based on antibody staining, is not evident. Moreover, HIM-5::GFP and HIM-5::HA look different from each other, and neither resembles the low-resolution images shown in Figure 6 in Meneely et al 2012, which showed nuclear staining throughout the germline, including in the mitotic zone, and also in somatic sheath cells. Given the differences in localization between the tagged transgenes and the endogenous protein, it is important to analyze the behavior of the endogenous, untagged protein. A minor issue: a wild-type control should also be shown for HIM-5::HA in Figure S4. 

Wild type control added to figure S4

Evidence that XND-1 and HIM-17 form a complex is weak; it is supported by the Y2H and co-IP data but opposed by functional analysis or localization. The diversity of proteins found in the Co-IP of HIM-17::GFP (Table S2) indicate that these interactions are unlikely to be specific. The independent localization of these proteins to chromatin is clear evidence that they do not form an obligate complex; additionally, they have been found to regulate distinct (although overlapping) sets of genes. The predicted structure generated by Alphafold3 has very low confidence and should not be taken as evidence for an interaction.The newly added argument about the lack of apparently overlap between HIM-17 and XND1 due to the distance between the HA tag on HIM-17 and XND-1 is flawed and should be removed - the extended C-terminus in the predicted AlphaFold3 C-terminus of HIM-17 has been interpreted as if it were a structured domain. Moreover, the predicted distance of 180 Å (18 nm) is comparable to the distance between a fluorophore on a secondary antibody and the epitope recognized by the primary antibody (~20-25 nm) and is far below than the resolution limit of light microscopy. 

We appreciate the reviewer’s thoughtful comment. The evidence supporting a physical interaction between XND-1 and HIM-17 is not only shown by our co-IP experiments, but it has also been recently shown in an independent study where MS analyses were conducted on HIM-17::3xHA pull downs to identify novel HIM-17 interactors (Blazickova et al.; 2025 Nature Comms). As shown in the data provided in this study, also under these experimental settings XND-1 was identified as a highly enriched putative HIM-17 interactor. We do acknowledge that their chromatin localization patterns are distinct and they regulate overlapping but not identical sets of genes, however, it is worth noting that protein–protein interactions in meiosis are often transient or context-dependent, and may not necessarily result in co-localization detectable by microscopy. In line with this, in the same work cited above, a similar situation for BRA-2 and HIM-17 was reported, as they were shown to interact biochemically despite the absence of overlapping staining patterns. 

Minor issues: 

The images shown in Panel D in Figure 1 seem to have very different resolutions; the HTP3/HIM-17 colocalization image is particularly blurry/low-resolution and should be replaced. The contrast between blue and green cannot be seen clearly; colors with stronger contrast should be used, and grayscale images should also be shown for individual channels. High-resolution images should probably be included for all of the factors analyzed here to facilitate comparisons.

Author response:

Reviewer #1:

We thank the reviewer for this important point. Beyond long reaction times, we did not originally exclude participants based on low EMA variability. We agree this is a relevant concern, particularly given the need to add small random noise to some EMA series for model convergence. In the revised manuscript, we will assess additional indicators of careless responding, including within-person EMA variability (e.g., standard deviation or proportion of modal responses) following Jaso et al., 2022 criteria. We will conduct sensitivity analyses excluding low-variability responses or participants and report whether these checks affect the robustness of the results. We will also clarify in the Discussion that minimal EMA variance may reflect either true affective stability or reduced engagement, and discuss how this ambiguity may affect interpretation.

Reviewer #2:

We thank the reviewer for raising this fundamental conceptual concern. We agree that more research is needed to fully understand the processes captured by DQRT. In the revised manuscript, we will more clearly reference and summarize prior validation work from our lab providing strong support for a cognitive characterization of DQRT as a measure of cognitive processing speed, while also explicitly acknowledging potential confounds and limitations (Teckentrup et al., 2025). We will clarify that our DQRT computation followed those validated procedures, including exclusion of extreme values above the sample-specific median + 2 SD. In addition, consistent with Reviewer #1’s comment, we will expand the Discussion of how potential careless responding and non-cognitive factors may influence DQRT. We will further tone down language implying causal inference.

References

Jaso, B. A., Kraus, N. I., & Heller, A. S. (2022). Identification of careless responding in ecological momentary assessment research: From posthoc analyses to real-time data monitoring. Psychological Methods, 27(6), 958.

Teckentrup, V., Rosická, A. M., Donegan, K. R., Gallagher, E., Hanlon, A. K., & Gillan, C. M. (2025). Digital questionnaire response time (DQRT): A ubiquitous and low-cost digital assay of cognitive processing speed. Behavior Research Methods, 57(7), 200.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Drosophila larval type II neuroblasts generate diverse types of neurons by sequentially expressing different temporal identity genes during development. Previous studies have shown that the transition from early temporal identity genes (such as Chinmo and Imp) to late temporal identity genes (such as Syp and Broad) depends on the activation of the expression of EcR by Seven-up (Svp) and progression through the G1/S transition of the cell cycle. In this study, Chaya and Syed examined whether the expression of Syp and EcR is regulated by cell cycle and cytokinesis by knocking down CDK1 or Pav, respectively, throughout development or at specific developmental stages. They find that knocking down CDK1 or Pav either in all type II neuroblasts throughout development or in single-type neuroblast clones after larval hatching consistently leads to failure to activate late temporal identity genes Syp and EcR. To determine whether the failure of the activation of Syp and EcR is due to impaired Svp expression, they also examined Svp expression using a Svp-lacZ reporter line. They find that Svp is expressed normally in CDK1 RNAi neuroblasts. Further, knocking down CDK1 or Pav after Svp activation still leads to loss of Syp and EcR expression. Finally, they also extended their analysis to type I neuroblasts. They find that knocking down CDK1 or Pav, either at 0 hours or at 42 hours after larval hatching, also results in loss of Syp and EcR expression in type I neuroblasts. Based on these findings, the authors conclude that cycle and cytokinesis are required for the transition from early to late temporal identity genes in both types of neuroblasts. These findings add mechanistic details to our understanding of the temporal patterning of Drosophila larval neuroblasts.

Strengths:

The data presented in the paper are solid and largely support their conclusion. Images are of high quality. The manuscript is well-written and clear.

We appreciate the reviewer’s detailed summary and recognition of the study’s strengths.

Weaknesses:

The quantifications of the expression of temporal identity genes and the interpretation of some of the data could be more rigorous.

(1) Expression of temporal identity genes may not be just positive or negative. Therefore, it would be more rigorous to quantify the expression of Imp, Syp, and EcR based on the staining intensity rather than simply counting the number of neuroblasts that are positive for these genes, which can be very subjective. Or the authors should define clearly what qualifies as "positive" (e.g., a staining intensity at least 2x background).

We thank the reviewer for this helpful suggestion. In the new version, we have now clarified how positive expression was defined and added more details of our quantification strategy to the Methods section (page 11, lines 380-388; lines 426-434 in tracked changes file). Fluorescence intensity for each neuroblast was normalized to the mean intensity of neighboring wild-type neuroblasts imaged in the same field. A neuroblast was considered positive for a given factor when its normalized nuclear intensity was at least 2× the local background. This scoring criterion was applied uniformly across all genotypes and time points. All quantifications were performed on the raw LSM files in Fiji prior to assembling the figure panels.

(2) The finding that inhibiting cytokinesis without affecting nuclear divisions by knocking down Pav leads to the loss of expression of Syp and EcR does not support their conclusion that nuclear division is also essential for the early-late gene expression switch in type II NSCs (at the bottom of the left column on page 5). No experiments were done to specifically block the nuclear division in this study specifically. This conclusion should be revised.

We blocked both cell cycle progression and cytokinesis, and both these manipulations affected temporal gene transitions, suggesting that both cell cycle and cytokinesis are essential. To our knowledge, no mechanism/tool exists that selectively blocks nuclear division while leaving cell cycle progression intact. We have added more clarification on page 4, line 123 onwards (lines 126 onwards in tracked changes file).

(3) Knocking down CDK1 in single random neuroblast clones does not make the CDK1 knockdown neuroblast develop in the same environment (except still in the same brain) as wild-type neuroblast lineages. It does not help address the concern whether "type 2 NSCS with cell cycle arrest failed to undergo normal temporal progression is indirectly due to a lack of feedback signaling from their progeny", as discussed (from the bottom of the right column on page 9 to the top of the left column on page 10). The CDK1 knockdown neuroblasts do not divide to produce progeny and thus do not receive a feedback signal from their progeny as wild-type neuroblasts do. Therefore, it cannot be ruled out that the loss of Syp and EcR expression in CDK1 knockdown neuroblasts is due to the lack of the feedback signal from their progeny. This part of the discussion needs to be clarification.

Thanks to the reviewer for raising this critical point. We agree and have added more clarification of our interpretations and limitations to our studies in the revised text on page 8, line 278-282 (lines 296-300 in tracked changes file)

(4) In Figure 2I, there is a clear EcR staining signal in the clone, which contradicts the quantification data in Figure 2J that EcR is absent in Pav RNAi neuroblasts. The authors should verify that the image and quantification data are consistent and correct.

When cytokinesis is blocked using pav-RNAi, the neuroblasts become extremely large and multinucleated. In some large pav RNAi clones, we observed a weak EcR signal near the cell membrane. However, more importantly, none of the nuclear compartments showed detectable EcR staining, where EcR is typically localized. We selected a representative nuclear image for the figure panel. To clarify this observation, we have now added an explanatory note to the discussion section on page 8, lines 283-291 (lines 301-309 in tracked changes file).

Reviewer #2 (Public review):

Summary:

Neural stem cells produce a wide variety of neurons during development. The regulatory mechanisms of neural diversity are based on the spatial and temporal patterning of neural stem cells. Although the molecular basis of spatial patterning is well-understood, the temporal patterning mechanism remains unclear. In this manuscript, the authors focused on the roles of cell cycle progression and cytokinesis in temporal patterning and found that both are involved in this process.

Strengths:

They conducted RNAi-mediated disruption on cell cycle progression and cytokinesis. As they expected, both disruptions affected temporal patterning in NSCs.

We appreciate the reviewer’s positive assessment of our experimental results.

Weaknesses:

Although the authors showed clear results, they needed to provide additional data to support their conclusion sufficiently.

For example, they need to identify type II NSCs using molecular markers (Ase/Dpn).The authors are encouraged to provide a more detailed explanation of each experiment. The current version of the manuscript is difficult for non-expert readers to understand.

Thanks for your feedback. We have now included a detailed description of how we identify type II NSCs in both wild-type and mutant clones. We have also added a representative Asense staining to clearly distinguish type 1 (Ase⁺) from type 2 (Ase^-) NSCs see Figure S1. We have also added a resources table explaining the genotypes associated with each figure, which was omitted due to an error in the previous version of the manuscript. 

Reviewer #3 (Public review):

Summary:

The manuscript by Chaya and Syed focuses on understanding the link between cell cycle and temporal patterning in central brain type II neural stem cells (NSCs). To investigate this, the authors perturb the progression of the cell cycle by delaying the entry into M phase and preventing cytokinesis. Their results convincingly show that temporal factor expression requires progression of the cell cycle in both Type 1 and Type 2 NSCs in the Drosophila central brain. Overall, this study establishes an important link between the two timing mechanisms of neurogenesis.

Strengths:

The authors provide solid experimental evidence for the coupling of cell cycle and temporal factor progression in Type 2 NSCs. The quantified phenotype shows an all-ornone effect of cell cycle block on the emergence of subsequent temporal factors in the NSCs, strongly suggesting that both nuclear division and cytokinesis are required for temporal progression. The authors also extend this phenotype to Type 1 NSCs in the central brain, providing a generalizable characterization of the relationship between cell cycle and temporal patterning.

We thank the reviewer for recognizing the robustness of our data linking the cell cycle to temporal progression.

Weaknesses:

One major weakness of the study is that the authors do not explore the mechanistic relationship between the cell cycle and temporal factor expression. Although their results are quite convincing, they do not provide an explanation as to why Cdk1 depletion affects Syp and EcR expression but not the onset of svp. This result suggests that at least a part of the temporal cascade in NSCs is cell-cycle independent, which isn't addressed or sufficiently discussed.

Thank you for bringing up this important point. We are equally interested in uncovering the mechanism by which the cell cycle regulates temporal gene transitions; however, such mechanistic exploration is beyond the scope of the present study. Interestingly, while the temporal switching factor Svp is expressed independently of the cell cycle, the subsequent temporal transitions are not. We have expanded our discussion on this intriguing finding (page 9, line 307-315; lines 345-355 in tracked changes file). Specifically, we propose that svp activation marks a cell-cycle–independent phase, whereas EcR/Syp induction likely depends on cell-cycle–coupled mechanisms, such as mitosis-dependent chromatin remodeling or daughter-cell feedback. Although further dissection of this mechanism lies beyond the current study, our findings establish a foundation for future work aimed at identifying how developmental timekeeping is molecularly coupled to cell-cycle progression.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) Figure 1 C and D, it would be better to put a question mark to indicate that these are hypotheses to be tested. 

We appreciate this suggestion and have added question marks in Figure 1C and 1D to clearly indicate that these panels represent hypotheses under investigation clearly.

(2) Figure 2A-I, Figure 4A-I, Figure 5A-I and K-S, in addition to enlarged views of single type II neuroblasts, it would be more convincing to include zoomed-out images of the entire larval brain or at least a portion of the brain to include neighboring wild-type type II neuroblasts as internal controls. Also, it would be ideal to show EcR staining from the same neuroblasts as IMP and Syp staining. 

We thank the reviewer for this valuable input. In our imaging setup, the number of available antibody channels was limited to four (anti-Ase, anti-GFP, anti-Syp, and antiImp). Adding EcR in the same sample was therefore not technically possible, we performed EcR staining separately. 

(3) The authors cited "Syed et al., 2024" (in the middle of the right column on page 5), but this reference is missing in the "References" section and should be added. 

The missing citation has been added to the reference section.  

(4) It would be better to include Ase staining in the relevant figure to indicate neuroblast identity as type I or type II. 

We agree and now include representative Ase staining for both type 1 and type 2 NSC clones in Figure S1, along with corresponding text updates that describe these markers.

Reviewer #2 (Recommendations for the authors): 

Major comments 

(1) The present conclusion relies on the results using Cdk1 RNAi and pav RNAi. It is still possible that Cdk1 and Pav are involved in the regulation of temporal patterning independent of the regulation of cell cycle or cytokinesis, respectively. To avoid this possibility, the authors need to inhibit cell cycle progression or cytokinesis in another alternative manner. 

We thank the reviewer for raising this important point. While we cannot completely exclude gene-specific, cell-cycle-independent roles for Cdk1 or Pav, we observe consistent phenotypes across several independent manipulations that slow or block the cell cycle. Also, earlier studies using orthogonal approaches that delay G1/S (Dacapo/Rbf) or impair mitochondrial OxPhos (which lengthens G1/S; van den Ameele & Brand, 2019) produce similar temporal delays. These concordant phenotypes strongly support the interpretation that altered cell-cycle progression—rather than specific roles of a single gene—is the primary cause of the defect. While we cannot exclude additional, gene-specific effects of Cdk1 or Pav, the concordant phenotypes across independent perturbations make the cell-cycle disruption model the most parsimonious interpretation. We have clarified this reasoning in the discussion section on pages 8-9, lines 293-305 (lines 311-343 in tracked changes file).

(2) To reach the present conclusion, the authors need to address the effects of acceleration of cell cycle progression or cytokinesis on temporal patterning. 

We thank the reviewer for this insightful suggestion. To our knowledge, there are currently no established genetic tools that can specifically accelerate cell-cycle progression in Drosophila neuroblasts. However, our results demonstrate that blocking the cell cycle impairs the transition from early to late temporal gene expression. These findings suggest that proper cell-cycle progression is essential for the transition from early to late temporal identity in neuroblasts.

Minor comments 

(3) P3L2 (right), ... we blocked the NSC cell cycle...

How did they do it? 

Which fly lines were used?

Why did they use the line? 

These details are now included in the Materials and Methods and the Resource Table (pages 11-13). We used Wor-Gal4, Ase-Gal80 to drive UAS-Cdk1RNAi and UASpavRNAi in type 2 NSCs 

(4) P5L1(left), ... we used the flip-out approach...

Why did they conduct it? 

Probably, the authors have reasons other than "to further ensure." 

We have clarified in the text on page 4, lines 137-139, that the flip-out approach was used to generate random single-cell clones, enabling quantitative analysis of type 2 NSCs within an otherwise wild-type brain. 

(5) P5L8(left), ... type 2 hits were confirmed by lack of the type 1 Asense...  The authors must examine Deadpan (Dpn) expression as well. Because there are a lot of Asense (Ase) negative cells in the brain (neurons, glial cell, and neuroepithelial cells). 

Type II NSCs can be identified as Dpn+/Ase- cells.

We agree that Dpn is a helpful marker. However, we reliably distinguished type II NSCs by their lack of Ase and larger cell size relative to surrounding neurons and glia, which are smaller in size and located deeper within the clone. These differences, together with established lineage patterns, allow unambiguous identification of type 2 NSCs across all genotypes. We have now added representative type I and type 2 NSC clones to the supplemental figure S1 (E-G’) with Asense stains to demonstrate how we differentiate type I from type II NSCs. 

(6) P5L32(left), To do this, we induced... 

This sentence should be made more concise.

Please rephrase it. 

The sentence has been rewritten for clarity and concision.

(7)  P5L42(left), ...lack of EcR/Syp expression (Figure 2).  However, EcR expression is still present (Figure 2I). 

In some large pavRNAi clones, a weak EcR signal can be observed near the cell membrane; however, none of the nuclear compartments—where EcR is typically localized—show detectable staining. We selected a representative nuclear image for the figure and addressed this observation on page 8, lines 283-291 (lines 301-309 in tracked changes file).

(8) P7L29(left), ......had persistent Imp expression...

Imp expression is faint compared to that in Figure 2G.

The differences between Figures 2G and 3G should be discussed. 

We thank the reviewer for this comment. We have added a note in the Methods section clarifying that brightness and contrast were adjusted per panel for optimal visualization; thus, apparent differences in signal intensity do not reflect biological variation. Fluorescence intensity for each neuroblast was normalized to the mean intensity of neighboring wild-type neuroblasts imaged in the same field. A neuroblast was considered Imp-positive when its normalized nuclear intensity was at least 2× the local background. This scoring criterion was applied uniformly across all genotypes and time points. All quantifications were performed on the raw LSM files in Fiji prior to assembling the figure panels.

(9) P8 (Figure 5)

The Imp expression is faint compared to that in Figure 5Q.

The difference between Figure 5G and 5Q should be discussed further. 

As mentioned above, we have clarified our image processing approach in the Methods section to explain any differences in signal appearance between these figures.

(10) P10 Materials and Methods

The authors did not mention the fly lines used. This is very important for the readers. 

We thank the reviewer for bringing this oversight to our attention. The Resource Table was inadvertently omitted from the initial submission. The complete list of fly lines and reagents used in this study is now provided in the updated Resource Table.

Reviewer #3 (Recommendations for the authors): 

Major points 

(1) The authors mention that the heat-shock induction at 42ALH is well after svp temporal window and therefore the cell cycle block independently affects Syp and EcR expression. However, Figure 3 shows svp-LacZ expression at 48ALH. If svp expression is indeed transient in Type 2 NSCs, then this must be validated using an immunostaining of the svp-LacZ line with svp antibody. This is crucial as the authors claim that cell cycle block doesn't affect does affect svp expression and is required independently. 

We thank the reviewer for bringing this important issue to our attention. As noted, Svp protein is expressed transiently and stochastically in type 2 NSCs (Syed et al., 2017), making direct antibody quantification challenging upon cell cycle block. Consistent with previous work (Syed et al., 2017), we used the svp-LacZ reporter line to visualize stabilized Svp expression, which reliably captures Svp expression in type 2 NSCs (Syed et al., 2017 https://doi.org/10.7554/eLife.26287, and Dhilon et al., 2024 https://doi.org/10.1242/dev.202504).

(2) The authors have successfully slowed down the cell cycle and showed that it affects temporal progression. However, a converse experiment where the cell cycle is sped up in NSCs would be an important test for the direct coupling of temporal factor expression and cell cycle, wherein the expectation would be the precocious expression of late temporal factors in faster cycle NSCs. 

We agree that such an experiment would be ideal. However, as noted above (Reviewer #2 comment 2), to our knowledge, no suitable tools currently exist to accelerate neuroblast cell-cycle progression without pleiotropic effects.

Minor point 

The authors must include Ray and Li (https://doi.org/10.7554/eLife.75879) in the references when describing that "...cell cycle has been shown to influence temporal patterning in some systems,...".  

We thank the reviewer for this helpful suggestion. The cited reference (Ray and Li, eLife, 2022) has now been included and appropriately referenced in the revised manuscript.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews: 

Reviewer #1 (Public review): 

Petrovic et al. investigate CCR5 endocytosis via arrestin 2, with a particular focus on clathrin and AP2 contributions. The study is thorough and methodologically diverse. The NMR titration data clearly demonstrate chemical shift changes at the canonical clathrin-binding site (LIELD), present in both the 2S and 2L arrestin splice variants. 

To assess the effect of arrestin activation on clathrin binding, the authors compare: truncated arrestin (1-393), full-length arrestin, and 1-393 incubated with CCR5 phosphopeptides. All three bind clathrin comparably, whereas controls show no binding. These findings are consistent with prior crystal structures showing peptide-like binding of the LIELD motif, with disordered flanking regions. The manuscript also evaluates a non-canonical clathrin binding site specific to the 2L splice variant. Though this region has been shown to enhance beta2-adrenergic receptor binding, it appears not to affect CCR5 internalization. 

Similar analyses applied to AP2 show a different result. AP2 binding is activation-dependent and influenced by the presence and level of phosphorylation of CCR5-derived phosphopeptides. These findings are reinforced by cellular internalization assays. 

In sum, the results highlight splice-variant-dependent effects and phosphorylation-sensitive arrestin-partner interactions. The data argue against a (rapidly disappearing) one-size-fitsall model for GPCR-arrestin signaling and instead support a nuanced, receptor-specific view, with one example summarized effectively in the mechanistic figure.

We thank the referee for this positive assessment of our manuscript. Indeed, by stepping away from the common receptor models for understanding internalization (b2AR and V2R), we revealed the phosphorylation level of the receptor as a key factor in driving the sequestration of the receptor from the plasma membrane. We hope that the proposed mechanistic model will aid further studies to obtain an even more detailed understanding of forces driving receptor internalization.

Weaknesses: 

Figure 1 shows regions alphaFold model that are intrinsically disordered without making it clear that this is not an expected stable position. The authors NMR titration data are n=1. Many figure panels require that readers pinch and zoom to see the data.

In the “Recommendations for the Authors” section, we addressed the reviewer’s stated weaknesses. In short, for the AlphaFold representation in Figure 1A, we added explicit labeling and revised the legend and main text to clearly state that the depicted loops are intrinsically disordered, absent from crystal structures due to flexibility, and shown only for visualization of their location. We also clarified that the NMR titration experiments inherently have n = 1 due to technical limitations, and that this is standard practice in the field, while ensuring individual data points remain visible. The supplementary NMR figures now have more vibrant coloring, allowing easier data assessment. However, we have not changed the zooming of the microscopy and NMR spectra. We believe that the presentation of microscopy data, which already show zoomed-in regions of interest, follow standard practices in the field. Furthermore, we strongly believe that we should display full NMR spectra in the supplementary figures to allow the reader to assess the overall quality and behavior. As indicated previously, the reader can zoom in to very high resolution, since the spectra are provided by vector graphics. Zoomed regions of the relevant details are provided in the main figures.

Reviewer #2 (Public review): 

Summary: 

Based on extensive live cell assays, SEC, and NMR studies of reconstituted complexes, these authors explore the roles of clathrin and the AP2 protein in facilitating clathrin mediated endocytosis via activated arrestin-2. NMR, SEC, proteolysis, and live cell tracking confirm a strong interaction between AP2 and activated arrestin using a phosphorylated C-terminus of CCR5. At the same time a weak interaction between clathrin and arrestin-2 is observed, irrespective of activation. 

These results contrast with previous observations of class A GPCRs and the more direct participation by clathrin. The results are discussed in terms of the importance of short and long phosphorylated bar codes in class A and class B endocytosis. 

Strengths: 

The 15N,1H and 13C,methyl TROSY NMR and assignments represent a monumental amount of work on arrestin-2, clathrin, and AP2. Weak NMR interactions between arrestin-2 and clathrin are observed irrespective of activation of arrestin. A second interface, proposed by crystallography, was suggested to be a possible crystal artifact. NMR establishes realistic information on the clathrin and AP2 affinities to activated arrestin with both kD and description of the interfaces.

We sincerely thank the referee for this encouraging evaluation of our work and appreciate the recognition of the NMR efforts and insights into the arrestin–clathrin–AP2 interactions.

Weaknesses: 

This reviewer has identified only minor weaknesses with the study. 

(1) I don't observe two overlapping spectra of Arrestin2 (1393) +/- CLTC NTD in Supp Figure 1

We believe the referee is referring to Figure 1 – figure supplement 2. We have now made the colors of the spectra more vibrant and used different contouring to make the differences between the two spectra clearer. The spectra are provided as vector graphics, which allows zooming in to the very fine details.

(2) Arrestin-2 1-418 resonances all but disappear with CCR5pp6 addition. Are they recovered with Ap2Beta2 addition and is this what is shown in Supp Fig 2D

We believe the reviewer is referring to Figure 3 - figure supplement 1. In this figure, the panels E and F show resonances of arrestin2^1-418 (apo state shown with black outline) disappear upon the addition of CCR5pp6 (arrestin2^1-418•CCR5pp6 complex spectrum in red). The panels C and D show resonances of arrestin2^1-418 (apo state shown with black outline), which remain unchanged upon addition of AP2b2 ^701-937 (orange), indicating no complex formation. We also recorded a spectrum of the arrestin2^1-418•CCR5pp6 complex under addition of AP2b2 ^701-937 (not shown), but the arrestin2 resonances in the arrestin2^1-418 •CCR5pp6 complex were already too broad for further analysis. This had been already explained in the text.

“In agreement with the AP2b2 NMR observations, no interaction was observed in the arrestin2 methyl and backbone NMR spectra upon addition of AP2b2 in the absence of phosphopeptide (Figure 3-figure supplement 1C, D). However, the significant line broadening of the arrestin2 resonances upon phosphopeptide addition (Figure 3-figure supplement 1E, F) precluded a meaningful assessment of the effect of the AP2b2 addition on arrestin2 in the presence of phosphopeptide”.

(3) I don't understand how methyl TROSY spectra of arrestin2 with phosphopeptide could look so broadened unless there are sample stability problems?

We thank the referee for this comment. We would like to clarify that in general a broadened spectrum beyond what is expected from the rotational correlation time does not necessarily correlate with sample stability problems. It is rather evidence of conformational intermediate exchange on the micro- to millisecond time scale.

The displayed ¹H-¹⁵N spectra of apo arrestin2 already suffer from line broadening due to such intrinsic mobility of the protein. These spectra were recorded with acquisition times of 50 ms (¹⁵N) and 55 ms (¹H) and resolution-enhanced by a 60˚-shifted sine-bell filter for ¹⁵N and a 60˚-shifted squared sine-bell filter for ¹H, respectively, which leads to the observed resolution with still reasonable sensitivity. The ¹H-¹⁵N resonances in Fig. 1b (arrestin2^1-393) look particularly narrow. However, this region contains a large number of flexible residues. The full spectrum, e.g. Figure 1-figure supplement 2, shows the entire situation with a clear variation of linewidths and intensities. The linewidth variation becomes stronger when omitting the resolution enhancement filters.

The addition of the CCR5pp6 phosphopeptide does not change protein stability, which we assessed by measuring the melting temperature of arrestin2^1-418 and arrestin2^1-418•CCR5pp6 complex (Tm = 57°C in both cases). We believe that the explanation for the increased broadening of the arrestin2 resonances is that addition of the CCR5pp6, possibly due to the release of the arrestin2 strand b20, amplifies the mentioned intermediate timescale protein dynamics. This results in the disappearance of arrestin2 resonances.

We have now included the assessment of arrestin2^1-418 and arrestin2^1-418•CCR5pp6 stability in the manuscript:

“The observed line broadening of arrestin2 in the presence of phosphopeptide must be a result of increased protein motions and is not caused by a decrease in protein stability, since the melting temperature of arrestin2 in the absence and presence of phosphopeptide are identical (56.9 ± 0.1 °C)”.

(4) At one point the authors added excess fully phosphorylated CCR5 phosphopeptide (CCR5pp6). Does the phosphopeptide rescue resolution of arrestin2 (NH or methyl) to the point where interaction dynamics with clathrin (CLTC NTD) are now more evident on the arrestin2 surface?

Unfortunately, when we titrate arrestin2 with CCR5pp6 (please see Isaikina & Petrovic et. al, Mol. Cell, 2023 for more details), the arrestin2 resonances undergo fast-to-intermediate exchange upon binding. In the presence of phosphopeptide excess, very few resonances remain, the majority of which are in the disordered region, including resonances from the clathrin-binding loop. Due to the peak overlap, we could not unambiguously assign arrestin2 resonances in the bound state, which precluded our assessment of the arrestin2-clathrin interaction in the presence of phosphopeptide. We have made this now clearer in the paragraph ‘The arrestin2-clathrin interaction is independent of arrestin2 activation’

“Due to significant line broadening and peak overlap of the arrestin2 resonances upon phosphopeptide addition, the influence of arrestin activation on the clathrin interaction could not be detected on either backbone or methyl resonances “.

(5) Once phosphopeptide activates arrestin-2 and AP2 binds can phosphopeptide be exchanged off? In this case, would it be possible for the activated arrestin-2 AP2 complex to re-engage a new (phosphorylated) receptor?

This would be an interesting mechanism. In principle, this should be possible as long as the other (phosphorylated) receptor outcompetes the initial phosphopeptide with higher affinity towards the binding site. However, we do not have experiments to assess this process directly. Therefore, we rather wish not to further speculate.

(6) I'd be tempted to move the discussion of class A and class B GPCRs and their presumed differences to the intro and then motivate the paper with specific questions. 

We appreciate the referee’s suggestion and had a similar idea previously. However, as we do not have data on other class-A or class-B receptors, we rather don’t want to motivate the entire manuscript by this question.

(7) Did the authors ever try SEC measurements of arrestin-2 + AP2beta2+CCR5pp6 with and without PIP2, and with and without clathrin (CLTC NTD? The question becomes what the active complex is and how PIP2 modulates this cascade of complexation events in class B receptors.

We thank the referee for this question. Indeed, we tested whether PIP2 can stabilize the arrestin2•CCR5pp6•AP2 complex by SEC experiments. Unfortunately, the addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. The resolution of SEC experiments was not sufficient to distinguish arrestin2 in oligomeric form or in arrestin2•CCR5pp6•AP2 complex. We now mention this in the text:

“We also attempted to stabilize the arrestin2-AP2b2-phosphopetide complex through the addition of PIP2, which can stabilize arrestin complexes with the receptor (Janetzko et al., 2022). The addition of PIP2 increased the formation of arrestin2 dimers and higher oligomers, presumably due to the presence of additional charges. Unfortunately, the resolution of the SEC experiments was not sufficient to separate the arrestin2 oligomers from complexes with AP2b2”.

Reviewer #3 (Public review): 

Summary: 

Overall, this is a well-done study, and the conclusions are largely supported by the data, which will be of interest to the field. 

Strengths: 

Strengths of this study include experiments with solution NMR that can resolve high-resolution interactions of the highly flexible C-terminal tail of arr2 with clathrin and AP2. Although mainly confirmatory in defining the arr2 CBL376LIELD380 as the clathrin binding site, the use of the NMR is of high interest (Fig. 1). The 15N-labeled CLTC-NTD experiment with arr2 titrations reveals a span from 39-108 that mediates an arr2 interaction, which corroborates previous crystal data, but does not reveal a second area in CLTC-NTD that in previous crystal structures was observed to interact with arr2. 

SEC and NMR data suggest that full-length arr2 (1-418) binding with 2-adaptin subunit of AP2 is enhanced in the presence of CCR5 phospho-peptides (Fig. 3). The pp6 peptide shows the highest degree of arr2 activation, and 2-adaptin binding, compared to less phosphorylated peptide or not phosphorylated at all. It is interesting that the arr2 interaction with CLTC NTD and pp6 cannot be detected using the SEC approach, further suggesting that clathrin binding is not dependent on arrestin activation. Overall, the data suggest that receptor activation promotes arrestin binding to AP2, not clathrin, suggesting the

AP2 interaction is necessary for CCR5 endocytosis. 

To validate the solid biophysical data, the authors pursue validation experiments in a HeLa cell model by confocal microscopy. This requires transient transfection of tagged receptor (CCR5-Flag) and arr2 (arr2-YFP). CCR5 displays a "class B"-like behavior in that arr2 is rapidly recruited to the receptor at the plasma membrane upon agonist activation, which forms a stable complex that internalizes onto endosomes (Fig. 4). The data suggest that complex internalization is dependent on AP2 binding not clathrin (Fig. 5). 

The addition of the antagonist experiment/data adds rigor to the study. 

Overall, this is a solid study that will be of interest to the field.

We thank the referee for the careful and encouraging evaluation of our work. We appreciate the recognition of the solidity of our data and the support for our conclusions regarding the distinct roles of AP2 and clathrin in arrestin-mediated receptor internalization.

Recommendations for the authors: 

Reviewer #1 (Recommendations for the authors): 

I believe that the authors have made efforts to improve the accessibility to a broader audience. In a few cases, I believe that the authors response either did not truly address the concern or made the problem worse. I am grouping these as 'very strong opinions' and 'sticking point'. 

Very strong opinion 1: 

While data presentation is somewhat at the authors discretion, there were several figures where the presentation did not make the work approachable, including microscopy insets and NMR spectra. A suggestion to 'pinch and zoom' does not really address this. For the overlapping NMR spectra in supporting Figure 1, I actually -can- see this on zooming, but I did not recognize this on first pass because the colors are almost identical for the two spectra. This is an easy fix. Changing the presentation by coloring these distinctly would alleviate this. The Supplemental figure to Fig. 2 looks strange with pinch and zoom. But at the end of the day, data presentation where the reader is to infer that they must zoom in is not very approachable and may prevent readers from being able to independently assess the data. In this case, there doesn't seem to be a strong rationale to not make these panels easier to see at 100% size. 

We appreciate the reviewer’s thoughtful comments regarding figure accessibility and agree that data presentation should be clear and interpretable without requiring readers to zoom in extensively. However, we must note that the presentation of the microscopy data follows standard practices in the field and that the panels already include zoomed-in regions, which enable easier access to key results and observations.

Regarding the NMR data, we have revised Figure 1—figure supplement 2 and Figure 2— figure supplement 1 to match the presentation style of Figure 3—figure supplement 1, which the reviewer apparently found more accessible. We also made the colors of the spectra more vibrant, as the referee suggested. We would like to emphasize that it is absolutely necessary to display the full NMR spectra in order to allow independent assessment of signal assignment, data quality, and overall protein behavior. Zoomed regions of the relevant details are provided in the main figures.

Very strong opinion 2: 

The author's response to lack of individual data points and error bars is that this is an n=1 experiment. I do not believe this meets the minimum standard for best practices in the field.

We respectfully disagree with the reviewer’s assessment. The Figure already displays individual data points, as shown already in the initial submission. Performing NMR titrations with isotopically labeled protein samples is inherently resource-intensive, and single-sample (n = 1) experiments are widely accepted and routinely reported in the field. Numerous studies have used the same approach, including Rosenzweig et al., Science (2013); Nikolaev et al., Nat. Methods (2019); and Hobbs et al., J. Biomol. NMR (2022), as well as our own recent work (Isaikina & Petrovic et al., Mol. Cell, 2023). These studies demonstrate that such NMR-based affinity measurements, even when performed on a single sample, are highly reproducible, precise, and consistent with orthogonal evidence and across different sample conditions.

Sticking point:

Figure 1A - the alphaFold model of arrestin2L depicts the disordered loops as ordered. The depiction is misleading at best, and inaccurate in truth. To use an analogy, what the authors depict is equivalent to publishing an LLM hallucination in the text. Unlike LLMs, alphaFold will actually flag its hallucination with the confidence (pLDDT) in the output. Both for LLMs and for alphaFold, we are spending much time teaching our students in class how to use computation appropriately - both to improve efficiency but also to ensure accuracy by removing hallucinations.

The original review indicated that confidences needed to be shown and that this needed to be depicted in a way that clarifies that this is NOT a structural state of the loops. The newly added description ("The model was used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 Cdomain, which are not detected in the available crystal structures...) worsens the concern because it even more strongly implies that a 0 confidence computational output is a likely structural state. It also indicates that these regions were 'not detected' in crystal structures. These regions of arrestin are intrinsically disordered. AlphaFold (by it's nature) must put out something in terms of coordinates, even if the pLDDT suggests that the region cannot be predicted or is not in a stable position, which is the case here. In crystal structures, these regions are not associated with interpretable electron density, meaning that coordinates are omitted in these regions because adding them would imply that under the conditions used, the protein adopts a low energy structural state in this region. This region is instead intrinsically disordered. 

A good description of why showing disordered loops in a defined position is incorrect and how to instead depict disorder correctly is in Brotzakis et al. Nat communications 16, 1632 (2025) "AlphaFold prediction of structural ensembles of disordered proteins", where figures 3A, 4A, and 5A show one AlphaFold prediction colored by confidence and 3B, 4B and 5B are more accurate depictions of the structural ensemble. 

Coming back to the original comment "The AlphaFold model could benefit from a more transparent discussion of prediction confidence and caveats. The younger crowd (part of the presumed intended readership) tends to be more certain that computational output is 'true'...." Right now, the authors are still showing in Fig 1A a depiction of arrestin with models for the loops that are untrue. They now added text indicating that these loops are visualized in an AlphaFold prediction and 'true' but 'not detected in crystal structures'. There is no indication in the text that these are intrinsically disordered. The lack of showing the pLDDT confidence and the lack of any indication that these are disordered regions is simply incorrect. 

We appreciate the concern of the reviewer towards AlphaFold models. As NMR spectroscopists we are highly aware of intrinsic biomolecular motions. However, our AlphaFold2 model is used as a graphical representation to display the interaction sites of loops; it is not intended to depict the loops as fixed structural states. The flexibility of the loops had been clearly described in the main text before:

“Arrestin2 consists of two consecutive (N- and C-terminal) β-sandwich domains (Figure 1A), followed by the disordered clathrin-binding loop (CBL, residues 353–386), strand b20 (residues 386–390), and a disordered C-terminal tail after residue 393”.

and

“Figure 1B depicts part of a 1H-15N TROSY spectrum (full spectrum in Figure 1-figure supplement 2A) of the truncated 15N-labeled arrestin2 construct arrestin21-393 (residues 1393), which encompasses the C-terminal strand β20, but lacks the disordered C-terminal tail. Due to intrinsic microsecond dynamics, the assignment of the arrestin21-393 1H-15N resonances by triple resonance methods is largely incomplete, but 16 residues (residues 367381, 385-386) within the mobile CBL could be assigned. This region of arrestin is typically not visible in either crystal or cryo-EM structures due to its high flexibility”.

as well as in the legend to Figure 1:

“The model was used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available crystal structures of apo arrestin2 [bovine: PDB 1G4M (Han et al., 2001), human: PDB 8AS4 (Isaikina et al., 2023)]. In the other structured regions, the model is virtually identical to the crystal structures”.

We have now further added a label ‘AlphaFold2 model’ to Figure 1A and amended the respective Figure legend to

“The model was used to visualize the clathrin-binding loop and the 344-loop of the arrestin2 C-domain, which are not detected in the available crystal structures of apo arrestin2 [bovine: PDB 1G4M (Han et al., 2001), human: PDB 8AS4 (Isaikina et al., 2023)] due to flexibility. In the other structured regions, the model is virtually identical to the crystal structures”.

Reviewer #2 (Recommendations for the authors): 

I appreciated the response by the authors to all of my questions. I have no further comments

We thank the referee for the raised questions, which we believe have improved the quality of the manuscript.

Author response:

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

We sincerely thank all three reviewers for their constructive comments. We deeply appreciate the reviewers’ efforts in summarizing our study, highlighting its strengths, and providing constructive suggestions. To enhance the quality and clarity of our work, we plan to address the concerns raised by the reviewers.

First, as Reviewer #1 suggested, we will note that clearer expression patterns of Wnt10b and Fgf2 may be detectable in scRNA-seq analyses at other stages, and we will also clarify that low-level signals of epithelial and CT/fibroblast markers outside their expected clusters may reflect technical bias. In addition, we agree with the reviewer’s point that our unsuccessful ISH experiments and the low abundance detected by RT-qPCR do not demonstrate absence of expression, and that conclusions from reanalyzing the Li et al. scRNA-seq dataset can depend strongly on analytical choices; therefore, while we focused on the 7 dpa sample because our RT-qPCR data suggested that Wnt10b and Fgf2 may be most enriched around the MB stage (the original study refers to 7 dpa as MB), we will explicitly acknowledge that analyzing a single time point—especially one with a low representation of epithelial cells—may yield incomplete or stage-biased interpretations, and that inclusion of additional time points could reveal clearer and potentially different expression patterns. We will also temper our wording regarding the inferred cellular sources to avoid over-interpretation based on the current data.

Second, to mitigate the concerns raised by Reviewer #3 regarding the generalization of our conclusions to amputation-induced (normal) limb regeneration, we will cite a previous study suggesting that ALM was used as the alternative experimental system for studying limb regeneration (Nacu et al., 2016, Nature, PMID: 27120163; Satoh et al., 2007, Developmental Biology, PMID: 17959163). We are confident that our ALM-based data provide a reasonable basis for understanding limb regeneration. We agree that there are important remaining questions—such as which cell populations express Wnt10b and Fgf2 and how endogenous WNT10B and FGF2 signals induce Shh expression in normal regeneration—which should be investigated in future studies to deepen our understanding of limb regeneration.

We also appreciate Reviewer #2’s careful evaluation of the technical rigor and quantification. We have benefited from the reviewer’s earlier feedback, which guided revisions that improved the manuscript’s rigor and presentation.

We are grateful for the reviewers’ insights and are confident that these revisions will significantly strengthen our manuscript.

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

Recommendations for the authors:

Reviewing Editor Comments:

The authors should be commended for addressing this gap - how cues from the DV axis interact with the AP axis during limb regeneration. Overall, the concept presented in this manuscript is extremely interesting and could be of high value to the field. However, the manuscript in its current form is lacking a few important data and resolution to fully support their conclusions, and the following needs to be addressed before publication:

(1) ISH data on Wnt10b and FGF2 from various regeneration time points are essential to derive the conclusion. Preferably multiplex ISH of Wnt10b/Fgf2/Shh or at least canonical ISH on serial sections to demonstrate their expression in dermis/epidermis and order of gene expression i.e. Shh is only expressed after expression of Wnt10b/FGF2. It would certainly help if this can also be shown in regular blastema.

We are grateful for the constructive suggestion on assessing Wnt10b and Fgf2 expression during regular regeneration, and we agree that clarifying their expression patterns in regular blastemas is important for strengthening the conclusions of our study. Because we cannot currently ensure sufficient sensitivity with multiplex FISH in our laboratory—partly due to high background—, we conducted conventional ISH on serial sections of regular blastemas at several time points (Fig. S5A). However, the expression patterns of Wnt10b and Fgf2 were not clear. To complement the ISH results, we performed RT-qPCR on microdissected dorsal and ventral halves of regular blastemas at the MB stage (Fig. S5B). We found that Wnt10b and Fgf2 were expressed at significantly higher levels in the dorsal and ventral halves, respectively, compared to the opposite half. This dorsal/ventral biased expression of Wnt10b/Fgf2 is consistent with our RNA-seq data. We further quantified expression levels of Wnt10b, Fgf2, and Shh across stages (intact, EB, MB, LB, and ED) and found that Wnt10b and Fgf2 peaked at the MB stage, whereas Shh peaked at the LB stage—consistent with the editor’s request regarding the order of gene expression (Fig. S5C). This temporal offset in upregulation supports our model. These results are now included in the revised manuscript (Line 294‒306).

To identify the cell types expressing Wnt10b or Fgf2, we analyzed published single-cell RNA-seq data (7 dpa blastema (MB), Li et al., 2021). As a result, Fgf2 expression was observed in the mesenchymal cluster, whereas Wnt10b expression was observed in both mesenchymal and epithelial clusters (Fig. S6). However, because only a small fraction of cells expressed Wnt10b, the principal cellular source of WNT10B protein remains unclear. The apparent low abundance likely contributes to the weak ISH signals and reflects current technical limitations. In addition, Wnt10b and Fgf2 expression did not follow Lmx1b expression (Fig. S6J, K), and Wnt10b and Fgf2 themselves were not exclusive (Fig. S6L). These results are now included in the revised manuscript (Line 307‒321). Together with the RT-qPCR data (Fig. S5B), these results suggest that Wnt10b and Fgf2 are not exclusively confined to purely dorsal or ventral cells at the single-cell level, even though they show dorsoventral bias when assessed in bulk tissue. These results suggest that Wnt10b/Fgf2 expression is not restricted to dorsal/ventral cells but mediated by dorsal/ventral cells, and co-existence of both signals should provide a permissive environment for Shh induction. Defining the precise spatial patterns of Wnt10b and Fgf2 in regular regeneration will therefore be an important goal for future work.  

(2) Validation of the absence of gene expression via qRT PCR in the given sample will increase the rigor, as suggested by reviewers.

We thank for this important suggestion and agree that validation by qRT-PCR increases the rigor of our study. Accordingly, we performed RT-qPCR on AntBL, PostBL, DorBL, and VentBL to corroborate the ISH results. The results are now included in Fig. 2. We also verified by RT-qPCR that Shh expression following electroporation and the quantitative results are now provided in Fig. 5.

(3) Please increase n for experiments where necessary and mention n values in the figures.

We thank for this helpful comment and agree on the importance of providing sufficient sample sizes. Accordingly, we increased the n for the relevant experiments and have indicated the n values in the corresponding figure legends.

(4) Most comments by all three reviewers are constructive and largely focus on improving the tone and language of the manuscript, and I expect that the authors should take care of them.

We thank the reviewers for their constructive feedback on the tone and language of the manuscript. We have carefully revised the text according to each comment, and we hope these modifications have improved both clarity and readability.

In addition, in revising the manuscript we also refined the conceptual framework. Our new analysis of Wnt10b and Fgf2 expression during normal regeneration suggests that these genes are not expressed in a strictly dorsal- or ventral-specific manner at the single-cell level. When these observations are considered together with (i) the RNA-seq comparison of dorsally and ventrally induced ALM blastemas, (ii) RT-qPCR of microdissected dorsal and ventral halves of regenerating blastemas, and (iii) the functional electroporation experiments, our interpretation is that Wnt10b and Fgf2 act as dorsal- and ventral-mediated signals, respectively: their production is regulated by dorsal or ventral cells, and the presence of both signals is required to induce Shh expression. Given those, we now think our conclusion might be explained without using the confusing term, “positional cue”. Because the distinction between “positional cue” and “positional information” could be confusing as noted by the reviewers, we rewrote our manuscript without using “positional cue.”

Reviewer #1 (Recommendations for the authors):

(1) Line 61: More explanation for what a double-half limb means is needed.

We thank the reviewer for this suggestion. We have revised the manuscript (Line 73‒76). Specifically, we now explain that a double-dorsal limb, for example, is a chimeric limb generated by excising the ventral half and replacing it with a dorsal half from the contralateral limb while preserving the anteroposterior orientation.

(2) Line 63-65: "Such blastemas form hypomorphic, spike-like structures or fail to regenerate entirely." This statement does not represent the breadth of work on the APDV axis in limb regeneration. The cited Bryant 1976 reference tested only double-posterior and double-anterior newt limbs, demonstrating the importance of disposition along the AP axis, not DV. Others have shown that the regeneration of double-half limbs depends upon the age of the animal and the length of time between the grafting of double-half limbs and amputation. Also, some double-dorsal or double-ventral limbs will regenerate complete AP axes with symmetrical DV duplications (Burton, Holder, and Jesani, 1986). Also, sometimes half dorsal stylopods regenerate half dorsal and half ventral, or regenerate only half ventral, suggesting there are no inductive cues across the DV axis as there are along the AP axis. Considering this is the basis of the study under question, more is needed to convince that the DV axis is necessary for the generation of the AP axis.

We thank the reviewer for this detailed and constructive comment. We acknowledge that previous studies have reported a range of outcomes for double-half limbs. For example, Burton et al. (1986) described regeneration defects in double-dorsal (DD) and double-ventral (VV) limbs, although limb patterning did occur in some cases (Burton et al., 1986, Table 1). As the reviewer notes, regenerative outcomes depend on variables such as animal age and the interval between construction of the double-half limb and amputation, sometimes called the effect of healing time (Tank and Holder, 1978). Moreover, variability has been reported not only in DD/VV limbs but also in double-anterior (AA) and double-posterior (PP) limbs (e.g., Bryant, 1976; Bryant and Baca, 1978; Burton et al., 1986). In the revised manuscript, we have therefore modified the statement to avoid over-generalization and to emphasize that regeneration can be incomplete under these conditions (Line 76‒82). Importantly, in order to provide the additional evidence requested and to directly re-evaluate whether dorsal and ventral cells are required for limb patterning, we performed the ALM experiments shown in Fig. 1. The ALM system allows us to assess this question in a binary manner (regeneration vs. non-regeneration), thereby strengthening the rationale for our conclusions regarding the necessity of the APDV orientations. We also revised a sentence at the beginning of the Results section to emphasize this point (Line 139‒140).

(3) Line 71: These findings suggest that specific signals from all four positional domains must be integrated for successful limb patterning, such that the absence of any one of them leads to failure." I was under the impression that half posterior limbs can grow all elements, but half anterior can only grow anterior elements.

We thank the reviewer for this helpful clarification. As summarized by Stocum, half-limb experiments show that while some digit formation can occur, limb patterning remains incomplete in both anterior-half and posterior-half limbs in some cases (Stocum, 2017). We see this point as closely related to the broader question of whether proper limb patterning requires the integration of signals from all four positional domains. As noted in our response above, our ALM experiments in Fig. 1 were designed to test this point directly, and our data support the interpretation that cells from all four orientations are necessary for correct limb patterning.

(4) Line 79-81: This is stated later in lines 98-105. I suggest expanding here or removing it here.

We thank the reviewer for this suggestion. In the original version, lines 79–81 introduced our use of the terms “positional cue” and “positional information,” and this content partially overlapped with what later appeared in lines 98–105. In the revised manuscript, we have substantially rewritten this section (Line 82‒84), including the sentences corresponding to lines 79–81 in the original version, to remove the term “positional cue,” as explained in our response to the Editor’s comment (4); our revision reflects new analyses indicating that Wnt10b and Fgf2 appear not be strictly restricted to dorsal or ventral cell populations, and we now describe these factors as dorsal- or ventral-mediated signals that act across dorsoventral domains to induce Shh expression. Accordingly, we no longer maintain the original use of “positional cue” and “positional information.”

(5) Line 92 - 93: "Similarly, an ALM blastema can be induced in a position-specific manner along the limb axes. In this case, the induced ALM blastema will lack cells from the opposite side." This sentence is difficult to follow. Isn't it the same thing stated in lines 88-90?

We thank the reviewer for this comment. We revised the sentence to improve readability and to avoid redundancy with original Lines 88–90 (Line 104‒106).

(6) Line 107: I think the appropriate reference is McCusker et al., 2014 (Position-specific induction of ectopic limbs in non-regenerating blastemas on axolotl forelimbs), although Vieira et al., 2019 can be included here. In addition, Ludolph et al 1990 should be cited.

We thank the reviewer for this suggestion. We have added McCusker et al. (2014) and Ludolph et al. (1990) as references in the revised manuscript (Line 120‒121).

(7) Line 107-109: A missing point is how the ventral information is established in the amniote limb. From what I remember, it is the expression of Engrailed 1, which inhibits the ventral expression of Wnt7a, and hence Lmx1b. This would suggest that there is no secreted ventral cue. This is a relatively large omission in the manuscript.

We thank the reviewer for this comment. We agree that ventral fate in amniotes is specified by En1 in the ventral ectoderm, which represses Wnt7a and thereby prevents induction of Lmx1b; accordingly, a secreted ventral morphogen analogous to dorsal Wnt7a has not been established. We added this point to the revised Introduction (Line 61‒64).

By contrast, in axolotl limb regeneration, our previous work on Lmx1b expression suggests that DV identities reflect the original positional identity rather than being re-specified during regeneration (Yamamoto et al., 2022). Within this framework, our original use of the term “ventral positional cue” does not imply a ventral patterning morphogen in the amniote sense; rather, it denotes downstream signals induced by cells bearing ventral identity that are required for the blastema to form a patterned limb. This interpretation is consistent with classic studies on double-half chimeras and ectopic contacts between opposite regions (Iten & Bryant, 1975; Bryant & Iten, 1976; Maden, 1980; Stocum, 1982) as well as with our ALM data (Fig. 1). For this reason, we intentionally used the term “positional cues” to refer to signals provided by cells bearing ventral identity, which can be considered separable from the DV patterning mechanism itself, in the original text. As explained in our response to the Editor’s comment (4), we describe these signals as “signals mediated by dorsal/ventral cells,” rather than “positional cues” in the revised manuscript.

The necessity of dorsal- and ventral-mediated signals is supported by classic studies on the double-half experiment. In the non-regenerating cases, structural patterns along the anteroposterior axis appear to be lost even though both anterior and posterior cells should, in principle, be present in a blastema induced from a double-dorsal or double-ventral limbs. In limb development of amniotes, Wnt7a/Lmx1b or En-1 mutants show that limbs can exhibit anteroposterior patterning even when tissues are dorsalized or ventralized—that is, in the relative absence of ventral or dorsal cells, respectively (Riddle et al., 1995; Chen et al., 1998; Loomis et al., 1996). Taken together, axolotl limb regeneration, in which the presence of both dorsal and ventral cells plays a role in anteroposterior patterning, should differ from other model organisms. It is reasonable to predict the dorsal- and ventral-mediated signals in axolotl limb regeneration. We included this point in the revised manuscript (Line 82‒89). However, there is no evidence that these signals are secreted molecules. For this reason, we have carefully used the term “dorsal-/ventral-mediated signals” in the Introduction without implying secretion.

(8) Introduction - In general, the argument is a bit misleading. It is written as if it is known that a ventral cue is necessary, but the evidence from other animal models is lacking, from what I know. I may be wrong, but further argument would strengthen the reasoning for the study.

We thank the reviewer for this thoughtful comment. We agree that it should not read as if it is known that a ventral cue is necessary. In the revised Introduction, we have addressed this in several ways. First, as described in our response to comment (7), we now explicitly note that in amniote limb development ventral identity is specified by En1-mediated repression of Wnt7a, and that a secreted ventral morphogen equivalent to dorsal Wnt7a has not been established. Second, we removed the term “positional cue” and no longer present “ventral positional cue” as a defined entity. Instead, we use mechanistic phrasing such as “signals mediated by ventral cells” and “signals mediated by dorsal cells,” which does not assume that such signals are secreted morphogens or universally conserved. Third, we have reframed the role of dorsal- and ventral-mediated signals as a working hypothesis specific to axolotl limb regeneration, rather than as a general conclusion across model systems.

(9) Line 129: Remove "As mentioned before".

We thank the reviewer for this suggestion. We have removed the phrase “As mentioned before” in the revised manuscript (Line 143).

(10) Figure 1: Are Lmx1, Fgf8, and Shh mutually exclusive? Multiplexed FISH would provide this information, and is a relatively important question considering the strong claims in the study.

We thank the reviewer for raising this important point. As noted in our response to the editor’s comment, we cannot currently ensure sufficiently high detection sensitivity with multiplex FISH in our laboratory. However, based on previous reports (Nacu et al., 2016), Fgf8 and Shh should be mutually exclusive. In contrast, with respect to Lmx1b, our analysis suggests that its expression is not mutually exclusive with either Fgf8 or Shh, at least their expression domains. To confirm this, we analyzed the published scRNA-seq data and the results were added to the supplemental figure 6. Fgf8 and Shh were expressed in both Lmx1b-positive and Lmx1b-negative cells (Fig. S6H, I), but Fgf8 and Shh themselves were mutually exclusive (Fig. S6M). This point is now included in the revised manuscript (Line 314‒317).

(11) Results section and Figure 2: More evidence is needed for the lack of Shh expression ISH in tissue sections. Demonstrating the absence of something needs some qPCR or other validation to make such a claim.

We thank the reviewer for this suggestion. We performed qRT-PCR on ALM blastemas to complement the ISH data (Fig. 2).

(12) Line 179: I think they are likely leucistic d/d animals and not wild-type animals based upon the images.

We thank the reviewer for this observation. In the revised manuscript, we have corrected the description to “leucistic animals” (Line 194).

(13) Line 183-186: I'm a bit confused about this interpretation. If Shh turns on in just a posterior blastema, wouldn't it turn on in a grafted posterior tissue into a dorsal or ventral region? Isn't this independent of environment, meaning Shh turns on if the cells are posterior, regardless of environment?

Our interpretation is that only posterior-derived cells possess the competency to express Shh. In other words, whether a cell is capable of expressing Shh depends on its original positional identity (Iwata et al., 2020), but whether it actually expresses Shh depends on the environment in which the cell is placed. The results of Fig. 3E and G indicate that Shh activation is dependent on environment and that the posterior identity is not sufficient to activate Shh expression. We have revised the manuscript to emphasize this distinction more clearly (Line 198‒203).

(14) Figure 4: Do the limbs have an elbow, or is it just a hand?

We thank the reviewer for this thoughtful question. From the appearance, an elbow-like structure can occasionally be seen; however, we did not examine the skeletal pattern in detail because all regenerated limbs used for this analysis were sectioned for the purpose of symmetry evaluation, and we therefore cannot state this conclusively. While this is indeed an important point, analyzing proximodistal patterning would require a very large number of additional experiments, which falls outside the main focus of the present study. For this reason, and also to minimize animal use in accordance with ethical considerations, we did not pursue further experiments here. In response to this point, we have added a description of the skeletal morphology of ectopic limbs induced by BMP2+FGF2+FGF8 bead implantation (Fig. 6). In these experiments, multiple ectopic limbs were induced along the same host limb. In most cases, these ectopic limbs did not show fusion with the proximal host skeleton, similar to standard ALM-induced limbs, although in one case we observed fusion at the stylopod level. We now note this observation in the revised manuscript (Line 347‒354).

We regard the relationship between APDV positional information and proximodistal patterning as an important subject for future investigation.

(15) Line 203 - 237: I appreciate the symmetry score to estimate the DV axis. Are there landmarks that would better suggest a double-dorsal or double-ventral phenotype, like was done in the original double-half limb papers?

We thank the reviewer for this thoughtful comment. In most cases, the limbs induced by the ALM exhibit abnormal and highly variable morphologies compared to normal limbs, making it difficult to apply consistent morphological landmarks as used in the original double-half limb studies. For this reason, we focused our analysis on “morphological symmetry” as a quantitative measure of DV axis patterning, and we have added this explanation to the manuscript (Line 232‒235). Additionally, we provided transverse sections along the proximodistal axis as supplemental figures (Figs. S2 and S4). In addition to reporting the symmetry score, we have explicitly stated in the text that symmetry was also assessed by visual inspection of these sections.

(16) Line 245-247: The experiment was done using bulk sequencing, so both the epithelium and mesenchyme were included in the sample. The posterior (Shh) and anterior (Fgf8) patterning cues are mesenchymally expressed. In amniotes, the dorsal cue has been thought to be Wnt7a from the epithelium. Can ISH, FISH, or previous scRNAseq data be used to identify genes expressed in the mesenchyme versus epithelium? This is very important if the authors want to make the claim for defining "The molecular basis of the dorsal and ventral positional cues" as was stated by the authors.

We thank the reviewer for highlighting this important point. As the reviewer notes, our bulk RNA-seq data do not distinguish between epithelial and mesenchymal expression domains. As noted in our response to the editor’s comment, we performed ISH and qPCR on regular blastemas. However, these approaches did not provide definitive information regarding the specific cell types expressing Wnt10b and Fgf2. To complement this, we re-analyzed publicly available single-cell RNA-seq data (from Li et al., 2021). As a results, Fgf2 was expressed mainly by the mesenchymal cells, and Wnt10b expression was observed in both mesenchymal and epithelial cells. These results are now included in the revised manuscript (Line 294‒321) and in supplemental figures (Fig. S6, S7).

(17) Was engrailed 1, lmx1b, or Wnt7a differentially expressed along the DV axis, suggesting similar signaling between? Are these expressed in mesenchyme? Previous work suggests Wnt7a is expressed throughout the mesenchyme, but publicly available scRNAseq suggests that it is expressed in the epithelium.

We thank the reviewer for this important comment. As noted, the reported expression patterns of DV-related genes are not consistent across studies, which likely reflects the technical difficulty of detecting these genes with high sensitivity. In our own experiments, expression of DV markers other than Lmx1b has been very weak or unclear by ISH. Whether these genes are expressed in the epithelium or mesenchyme also appears to vary depending on the detection method used. In our RNA-seq dataset, Wnt7a expression was detected at very low levels and showed no significant difference along the DV axis, while En1 expression was nearly absent. We have clarified these results in the revised manuscript (Line 437‒441). Our reanalysis of the published scRNA-seq likewise detected Wnt7a in only a very small fraction of cells. Accordingly, we consider it premature to reach a definitive conclusion—such as whether Wnt7a is broadly mesenchymal or restricted to epithelium—as suggested in prior reports. We also note that whether Wnt7a is epithelial or mesenchymal does not affect the conclusions or arguments of the present study. Although the roles of Wnt7a and En1 in axolotl DV patterning are certainly important, we feel that drawing a definitive conclusion on this issue lies beyond the scope of the present study, and we have therefore limited our description to a straightforward presentation of the data.

(18) Line 247-249: The sentence suggests that all the ligands were tried. This should be included in the supplemental data.

We thank the reviewer for this clarification. In fact, we tested only Wnt4, Wnt10b, Fgf2, Fgf7, and Tgfb2, and all of these results are presented in the figures. To avoid misunderstanding, we have revised the text to explicitly state that our analysis focused on these five genes (Line 272‒274).

(19) Line 249: An n =3 seems low and qPCR would be a more sensitive means of measuring gene induction compared to ISH. The ISH would confirm the qPCR results. Figure 5C is also not the most convincing image of Shh induction without support from a secondary method.

We have increased the sample size for these experiments (Line 277‒280). In addition, to complement the ISH results, we confirmed Shh induction by qPCR following electroporation of Wnt10b and Fgf2 (Fig. 5D, E). In addition, because Shh signal in the Wnt10b-electroporated VentBL images was particularly weak and difficult to discern, we replaced that panel with a representative example in which Shh signal is more clearly visible. These data are now included in the revised manuscript (Line 280‒282).

(20) Line 253: It is confusing why Wnt10b, but not Wnt4 would work? As far as I know, both are canonical Wnt ligands. Was Wnt7a identified as expressed in the RNAseq, but not dorsally localized? Would electroporation of Wnt7a do the same thing as Wnt10b and hence have the same dorsalizing patterning mechanisms as amniotes?

We thank the reviewer for raising this challenging but important question. Wnt10b was identified directly from our bulk RNA-seq analysis, as was Wnt4. The difference in the ability of Wnt10b and Wnt4 to induce Shh expression in VentBL may reflect differences in how these ligands activate downstream WNT signaling programs. WNT10B is a potent activator of the canonical WNT/β-catenin pathway (Bennett et al., 2005), although WNT10B has also been reported to trigger a β-catenin–independent pathway (Lin et al., 2021). By contrast, WNT4 can signal through both canonical and non-canonical (β-catenin–independent) pathways, and the balance between these outputs is known to depend on cellular context (Li et al., 2013; Li et al., 2019). Consistent with a requirement for canonical WNT signaling, we found that pharmacological activation of canonical WNT signaling with BIO (a GSK3 inhibitor) was also sufficient to induce Shh expression in VentBL. However, despite this, it is still unclear why Wnt10b, but not Wnt4, was able to induce Shh under our experimental conditions. One possible explanation is that different WNT ligands can engage the same receptors (e.g., Frizzled/LRP6) yet can drive distinct downstream transcriptional programs (This may depend on the state of the responding cells, as Voss et al. predicted), resulting in ligand-specific outputs (Voss et al., 2025). This point is now included in the revised discussion section (Line 402‒412). At present, we cannot distinguish between these possibilities experimentally, and we therefore refrain from making a stronger mechanistic claim.

With respect to Wnt7a, we detected Wnt7a expression at very low levels, and without a clear dorsoventral bias, in our RNA-seq analysis of ALM blastemas (we describe this point in Line 437‒440). This is consistent with previous work suggesting that axolotl Wnt7a is not restricted to the dorsal region in regeneration. Because of this low and unbiased expression, and because our data already implicated Wnt10b as a dorsal-mediated signal that can act across dorsoventral domains to permit Shh induction, we did not prioritize Wnt7a electroporation in the present study. We therefore cannot conclude whether Wnt7a would behave similarly to Wnt10b in this context.

Importantly, these uncertainties about ligand-specific mechanisms do not alter our main conclusion. Our data support the idea that a dorsal-mediated WNT signal (represented here by WNT10B and canonical WNT activation) and a ventral-mediated FGF signal (FGF2) must act together to permit Shh induction, and that the coexistence of these dorsal- and ventral-mediated signals is required for patterned limb formation in axolotl limb regeneration.

(21) Is canonical Wnt signaling induced after electroporation of Wnt10b or Wnt4? qPCR of Lef1 and axin is the most common way of showing this.

We thank the reviewer for this helpful suggestion. In addition to examining Shh expression, we also assessed canonical WNT signaling by qPCR analysis of Axin2 and Lef1 following Wnt10b electroporation. The data is now included in Fig. 5.

(22) Line 255-256: qPCR was presented for Figure 5D, but ISH was used for everything else. Is there a technical reason that just qPCR was used for the bead experiments?

We thank the reviewer for this helpful comment. In the original submission, our goal was to test whether treatment with commercial FGF2 protein or BIO could reproduce the results obtained by electroporation. In the revised manuscript, to avoid confusion between distinct experimental aims, we removed the FGF2–bead data from this section and instead used RT-qPCR to quantitatively corroborate Shh induction after electroporation (Fig. 5D–E). RT-qPCR provided a sensitive, whole-blastema readout and allowed a paired design (left limb: factor; right limb: GFP control) that increased statistical power while minimizing animal use. To address the reviewer’s point more directly, we additionally performed ISH for the BIO treatment and now include those results in Supplementary Figure 3 (Line 287‒288).

(23) Line 261-263: The authors did not show where Wnt10B or Fgf2 is expressed in the limb as claimed. The RNAseq was bulk, so ISH of these genes is needed to make this claim. Where are Wnt10b and Fgf2 expressed in the amputated limb? Do they show a dorsal (Wnt10b) and ventral (Fgf2) expression pattern?

We thank the reviewer for raising this important point. As noted in our response to the editor’s comment, we performed ISH on serial sections of regular blastemas at several time points (Fig. S5A). However, the expression patterns of Wnt10b and Fgf2 along the dorsoventral axis were not clear. To complement the ISH results, we performed RT-qPCR on microdissected dorsal and ventral halves of regular blastemas at the MB stage (Fig. S5B). We found that Wnt10b and Fgf2 were expressed at significantly higher levels in the dorsal and ventral halves, respectively, compared to the opposite half. This dorsal/ventral biased expression of Wnt10b/Fgf2 is consistent with our RNA-seq data. To identify the cell types expressing Wnt10b or Fgf2, we analyzed published single-cell RNA-seq data (7 dpa blastema (MB), Li et al., 2021). As a result, Fgf2 expression was observed in the mesenchymal cluster, whereas Wnt10b expression was observed in both mesenchymal and epithelial clusters (Fig. S6). However, because only a small fraction of cells expressed Wnt10b, the principal cellular source of WNT10B protein remains unclear. The apparent low abundance likely contributes to the weak ISH signals and reflects current technical limitations. In addition, Wnt10b and Fgf2 expression did not follow Lmx1b expression (Fig. S6J, K), and Wnt10b and Fgf2 themselves were not exclusive (Fig. S6L). Together with the RT-qPCR data (Fig. S5B), these results suggest that Wnt10b and Fgf2 are not exclusively confined to purely dorsal or ventral cells at the single-cell level, even though they show dorsoventral bias when assessed in bulk tissue, suggesting that Wnt10b/Fgf2 expression is not dorsal-/ventral-specific but mediated by dorsal/ventral cells. Defining the precise spatial patterns of Wnt10b and Fgf2 in regular regeneration will therefore be an important goal for future work. These points are now included in the revised manuscript (Line 485‒501).

(24) Line 266-288: The formation of multiple limbs is impressive. Do these new limbs correspond to the PD location they are generated?

We thank the reviewer for this interesting question. Interestingly, from our observations, there does appear to be a tendency for the induced limbs to vary in length depending on their PD location. The skeletal patterns of the induced multiple limbs are now included in Fig. 6. However, as noted earlier, the supernumerary limbs exhibit highly variable morphologies, and a rigorous analysis of PD correlation would require a large number of induced limbs. Since this lies outside the main focus of the present study, we have not pursued this point further in the manuscript.

(25) Line 288: The minimal requirement for claiming the molecular basis for DV signaling was identified is to ISH or multiplexed FISH for Wnt10b and Fgf2 in amputated limb blastemas to show they are expressed in the mesenchyme or epithelium and are dorsally and ventrally expressed, respectively. In addition, the current understanding of DV patterning through Wnt7a, Lmx1b, and En1 shown not to be important in this model.

We thank the reviewer for this comment and fully agree with the point raised. We would like to clarify that we are not claiming to have identified the molecular basis of DV patterning. As the reviewer notes, molecules such as Lmx1b, Wnt7a, and En1 are well identified in other animal models as key regulators of DV positional identity. There is no doubt that these molecules play central roles in DV patterning. However, in axolotl limb regeneration, clear DV-specific expression has not been demonstrated for these genes except for Lmx1b. Therefore, further studies will be required to elucidate the molecular basis of DV patterning in axolotls.

Our focus here is more limited: we aim to identify the molecular basis for the mechanisms in which positional domain-mediated signals (FGF8, SHH, WNT10B, and FGF2) regulate the limb patterning process, rather than the molecular basis of DV patterning. In fact, our results on Wnt10b and Fgf2 suggest that these genes did not affect dorsoventral identities.

We recognize that this distinction was not sufficiently clear in the original text, and we have revised the manuscript to describe DV patterning mechanisms in other animals and clarify that the dorsal- and ventral-mediated signals are distinct from DV patterning (Line 444‒450). At least, we avoid claiming that the molecular basis for DV signaling was identified.

(26) Line 335: References are needed for this statement. From what I found, Wnt4 can be canonical or non-canonical.

We thank the reviewer for this helpful comment. We have revised the manuscript (Line 404‒407). We added these citations at the relevant location and adjusted nearby wording to avoid implying pathway exclusivity, in alignment with our response to comment (20).

(27) Line 337-338: The authors cannot claim "that canonical, but not non-canonical, WNT signaling contributes to Shh induction" as this was not thoroughly tested is based upon the negative result that Wnt4 electroporation did not induce Shh expression.

We thank the reviewer for this important clarification. We agree that our data do not allow us to conclude that non-canonical WNT signaling in general does not contribute to Shh induction. Accordingly, we have removed the phrase “but not non-canonical” and revised the text to emphasize that, within the scope of our experiments, Shh induction was not observed following Wnt4 electroporation, whereas it was observed with Wnt10b.

(28) Line 345: In order to claim "WNT10B via the canonical WNT pathway...appears to regulate Shh expression" needs at least qPCR to show WNT10B induces canonical signaling.

We thank the reviewer for this comment. As noted in our response to comment (21), we also assessed canonical WNT signaling by qPCR analysis of Axin2 and Lef1 following Wnt10b electroporation (Line 282‒285).

(29) Lines 361-372: A few studies have been performed on DV patterning of the mouse digit regeneration in regards to Lmx1b and En1. It may be good to discuss how the current study aligns with these findings.

We appreciate the reviewer’s suggestion. As the reviewer refers, several studies have been performed on dorsoventral (DV) patterning in mouse digit tip regeneration in relation to Lmx1b and En1 (e.g., Johnson et al., 2022; Castilla-Ibeas et al., 2023). In the present study, however, our main conclusion is different in the scope of studies on mouse digit tip regeneration. We show that, in the axolotl, pre-existing dorsal and ventral identities (as reflected by dorsally derived and ventrally derived cells in the ALM blastema) are required together to induce Shh expression, and that this Shh induction in turn supports anteroposterior interaction at the limb level. This mechanism—dorsal-mediated and ventral-mediated signals acting in combination to permit Shh expression—does not have a clear direct counterpart in the mouse digit tip literature. Moreover, even with respect to Lmx1b, the two systems behave differently. In mouse digit tip regeneration, loss of Lmx1b during regeneration does not grossly affect DV morphology of the regenerate (Johnson et al., 2022). By contrast, in our axolotl ALM system, the presence or absence of Lmx1b-positive dorsal tissue correlates with the final dorsoventral organization of the induced limb-like structures (e.g., production of double-dorsal or double-ventral symmetric structures in the absence of appropriate dorsoventral contact). Thus, the role of dorsoventral identity in our model is directly tied to patterned limb outgrowth at the whole-limb scale, whereas in the mouse digit tip it has been reported primarily in the context of digit tip regrowth and bone regeneration competence, not robust DV repatterning (Johnson et al., 2022).

For these reasons, we believe that an extended discussion of mouse digit tip regeneration would risk implying a mechanistic equivalence between axolotl limb regeneration and mouse digit tip regeneration that is not supported by current data. Because the regenerative contexts differ, and because Lmx1b does not appear to re-establish DV patterning in the mouse regenerates (Johnson et al., 2022), we have chosen not to include an explicit discussion of mouse digit tip regeneration in the main text.

(30) Line 408-433: Although I appreciate generating a model, this section takes some liberties to tell a narrative that is not entirely supported by previous literature or this study. For example, lines 415-416 state "Wnt10b and Fgf2 are expressed at higher levels in dorsal and the ventral blastemal cells, respectively" which were not shown in the study or other studies.

We thank the reviewer for this important comment. We agree that the original model based on RNA-seq data overstated the evidence. To address this point experimentally, we examined Wnt10b and Fgf2 expression in regular blastemas (Supplemental Figure 5 and 6). Accordingly, our model is now framed as an inductive mechanism for Shh expression—supported by results in ALM (WNT10B in VentBL; FGF2 in DorBL) and by DV-biased expression. Concretely, the sentence previously paraphrased as “Wnt10b and Fgf2 are expressed at higher levels in dorsal and ventral blastemal cells, respectively” has been replaced with wording that (i) avoids single-cell DV specificity and (ii) emphasizes dorsal-/ventral-mediated regulation and the requirement for both signals to allow Shh induction (Line 510‒511).

Reviewer #2 (Recommendations for the authors):

(1) Introduction:

The authors' definitions of positional cues vs positional information are a little hard to follow, and do not appear to be completely accurate. From my understanding of what the authors explain, "positional information" is defined as a signal that generates positional identities in the regenerating tissue. This is a somewhat different definition than what I previously understood, which is the intrinsic (likely epigenetic) cellular identity associated with specific positional coordinates. On the other hand, the authors define "positional cues" as signals that help organize the cells according to the different axes, but don't actually generate positional identities in the regenerating cells. The authors provide two examples: Wnt7a as an example of positional information, and FGF8 as a positional cue. I think that coording to the authors definitions, FGF8 (and probobly Shh) are bone fide positional cues, since both signals work together to organize the regenerating limb cells - yet do not generate positional identities, because ectopic limbs formed from blastemas where these pathways have been activated do not regenerate (Nacu et al 2016). However, I am not sure Wnt7a constitutes an example of a "positional information" signal, since as far as I know, it has not been shown to generate stable dorsal limb identities (that remain after the signal has stopped) - at least yet. If it has, the authors should cite the paper that showed this. I think that some sort of diagram to help define these visually will be really helpful, especially to people who do not study regenerative patterning.

We thank the reviewer for this thoughtful comment. We now agree with the reviewer that our use of “positional cue” and “positional information” may have been confusing. In the revision—and as noted in our response to the Editor’s comment (4)—we have removed the term “positional cue” and no longer attempt to contrast it with “positional information.” Instead, we adopt phrasing that reflects our data and hypothesis: during limb patterning, dorsal-mediated signals act on ventral cells and ventral-mediated signals act on dorsal cells to induce Shh expression. This wording avoids implying that these signals specify dorsoventral identity.

Regarding WNT7A, we agree it has not been shown to generate a stable dorsal identity after signal withdrawal. In the revised Introduction we therefore describe WNT7A in amniote limb development as an extracellular regulator that induces Lmx1b in dorsal mesenchyme (with En1 repressing Wnt7a ventrally), rather than labeling it as “positional information” in a strict, identity-imprinting sense. We highlight this contrast because, in our axolotl experiments, WNT10B and FGF2 did not alter Lmx1b expression or dorsal–ventral limb characteristics when overexpressed, consistent with the idea that they act downstream of DV identity to enable Shh induction, not to establish DV identity.

(2) Results:

It would be helpful if the number of replicates per sample group were reported in the figure legends.

We thank the reviewer for this suggestion. In accordance with the comment, we have added the number of replicates (n) for each sample group in the figure legends.

Figure 2 shows ISH for A/P and D/V transcripts in different-positioned blastemas without tissue grafts. The images show interesting patterns, including the lack of Shh expression in all blastemas except in posterior-located blastemas, and localization of the dorsal transcript (Lmx1b) to the dorsal half of A or P located blastemas. My only concern about this data is that the expression patterns are described in only a small part of the ectopic blastema (how representative is it?) and the diagrams infer that these expression patterns are reflective of the entire blastema, which can't be determined by the limited field of view. It is okay if the expression patterns are not present in the entire blastema -in fact, that might be an important observation in terms of who is generating (and might be receiving) these signals.

We thank the reviewer for this insightful comment. Because Fgf8 and Shh expression was detectable only in a limited subset of cells, the original submission included only high-magnification images. In response to the reviewer’s valid concern about representativeness, we have now added low-magnification overviews of the entire blastema as a supplemental figure (Fig. S1) and clarified in the figure legend that these expression patterns can be focal rather than pan-blastemal (Line 795‒796).

In Figure 3, they look at all of these expression patterns in the grafted blastemas, showing that Shh expression is only visible when both D and V cells are present in the blastema. My only concern about this data is that the number of replicates is very low (some groups having only an N=3), and it is unclear how many sections the authors visualized for each replicate. This is especially important for the sample groups where they report no Shh expression -I agree that it is not observable in the single example sections they provide, but it is uncertain what is happening in other regions of the blastema.

We thank the reviewer for this important comment. To increase the reliability of the results, we have increased the number of biological replicates in groups where n was previously low. For all samples, we collected serial sections spanning the entire blastema. For blastemas in which Shh expression was observed, we present representative sections showing the signal. For blastemas without detectable Shh expression, we selected a section from the central region that contains GFP-positive cells for the Figure. To make these points explicit, we have added the following clarification to the Fig. 3 legend (Line 811‒815).

Figure 4: Shh overexpression in A/P/D/V blastemas - expression induces ectopic limbs in A/D/V locations. They analyzed the symmetry of these regenerates (assuming that Do and V located blastemas will exhibit D/V symmetry because they only contain cells from one side of that axis. I am a little concerned about how the symmetry assay is performed, since oblique sections through the digits could look asymmetric, while they are actually symmetric. It is also unclear how the angle of the boxes that the symmetry scores were based on was decided - I imagine that the score would change depending on the angle. It also appears that the authors picked different digits to perform this analysis on the different sample groups. I also admit that the logic of classification scheme that the authors used AI to perform their symmetry scoring analysis (both in Figures 4 and 5) is elusive to me. I think it would have been more informative if the authors leveraged the structural landmarks, like the localization of specific muscle groups. (If this experiment were performed in WT animals, the authors could have used pigment cell localization)... or generate more proximal sections to look at landmarks in the zeugopod.

We thank the reviewer for these detailed comments regarding the symmetry analysis. Because reliance on a computed symmetry score alone could raise the concerns noted by the reviewer, we now provide transverse sections along the proximodistal axis as supplemental figures (Figs. S2 and S4). These include levels corresponding to the distal end of the zeugopod and the proximal end of the autopod. In addition to reporting the symmetry score, we have explicitly stated in the text that symmetry was also assessed by visual inspection of these sections.

As also noted in our response to Reviewer #1 (comment 15), ALM-induced limbs frequently exhibit abnormal and highly variable morphologies, which makes it difficult to use consistent anatomical landmarks such as particular digits or muscle groups. For this reason, we focused our analysis on morphological symmetry rather than landmark-based metrics, and we emphasize this rationale in the revised text (Line 232‒235).

Regarding the use of bounding boxes, this procedure was chosen to minimize the effects of curvature or fixation-induced distortion. For each section, the box angle was adjusted so that the outer contour (epidermal surface) was aligned symmetrically; this procedure was applied uniformly across all conditions to avoid bias. We analyzed multiple biological replicates in each group, which helps mitigate potential artifacts due to oblique sectioning. To further reduce bias, we increased the number of fields included in the analysis to n = 24 per group in the revised version.

In addition, staining intensity varied among samples, such that a region identified as “muscle” in one sample could be assigned differently in another if classification were based solely on color. To avoid this problem, we used a machine-learning classifier trained separately for each sample, allowing us to group the same tissues consistently within that sample irrespective of intensity differences. In the context of ALM-induced limbs, where stable anatomical landmarks are not available, we consider this strategy the most appropriate. We have added this rationale to the revised manuscript for clarity (Line 239‒247).

Figure 5: The number of replicates in sample groups is relatively low and is quite variable between groups (ranging between 3 and 7 replicates). Zoom in to visualize Shh expression is small relative to the blastema, and it is difficult to discern why the authors positioned the window where they did, and how they maintained consistency among their different sample groups. In the examples of positive Shh expression - the signal is low and hard to see. Validating these expression patterns using some sort of quantitative transcriptional assay (like qRTPCR) would increase the rigor of this experiment ... especially given that they will be able to analyze gene expression in the entire blastema as opposed to sections that might not capture localized expression.

We thank the reviewer for this important comment. To increase the rigor of these experiments, we have increased the number of biological replicates in groups where n was previously low. In addition, because Shh signal in the Wnt10b-electroporated VentBL images was particularly weak and difficult to discern, we replaced that panel with a representative example in which Shh signal is more clearly visible. We also validated the Shh expression for Wnt10b–electroporated VentBL and Fgf2–electroporated DorBL by RT-qPCR, which assesses gene expression across the entire blastema. These results are now included in Fig. 5 and Line 280‒282. Finally, we clarified in the figure legend how the “window” for imaging was chosen: for samples with detectable Shh expression, the window was placed in the region where the signal was observed; for conditions without detectable Shh expression, the window was positioned in a comparable region containing GFP-positive cells (Line 836‒839). These revisions are included in the revised manuscript.

Figure 6: They treat dorsal and ventral wounds with gelatin beads soaked in a combination of BMP2+FGF8 (nerve factors) and FGF2 proposed ventral factor). Remarkably, they observe ectopic limb expression in only dorsal wounds, further supporting the idea that FGF2 provides the "ventral" signal. They show examples of this impressive phenotype on limbs with multiple ectopic structures that formed along the Pr/Di axis. Including images of tubulin staining (as they have in Figures 1 and 2) to ensure that the blastemas (or final regenerates) are devoid of nerves. The authors' whole-mount skeletal staining which shows fusion of the ectopic humerus with the host humerus, is a phenotype associated with deep wounding, which could provide an opportunity for more cellular contribution from different limb axes.

We thank the reviewer for these constructive comments. As noted in the prior study, when beads are used to induce blastemas without surgical nerve orientation, fine nerve ingrowth can still occur (Makanae et al., 2014), and the induced blastemas are not completely devoid of nerves. While it is still uncertain whether these recruited nerves are functional after blastema induction, it is an important point, and we added sentences about this in the revised manuscript (Line 341‒345).

Regarding the skeletal phenotype, despite careful implantation to avoid injuring deep tissues, bead-induced ectopic limbs on the dorsal side occasionally displayed fusion of the stylopod with the host humerus—a phenotype associated with deep wounding, as the reviewer notes. This observation suggests that contributions from a broader cellular population cannot be excluded. However, because fusion was observed in only 1 of 16 induced limbs analyzed, and because ectopic limbs induced at the forearm (zeugopod) level did not exhibit such fusion (n=1/6 for stylopod-level inductions; n=0/10 for zeugopod-level inductions), we believe that our main conclusion remains valid. Because fusion is not a typical outcome, we now present representative non-fusion cases—including zeugopod-origin examples—in the figure (Fig. 6L1, L2), and we report the fusion incidence explicitly in the text (Line 350‒354). We also note in the revised manuscript that stylopod fusion can occur in a minority of cases (Line 347‒349).

Figure 7 nicely summarizes their findings and model for patterning.

We thank the reviewer for this positive comment.

The table is cut off in the PDF, so it cannot be evaluated at this time.

In our copy of the PDF, the table appears in full, so this may have been a formatting issue. We have carefully checked the file and ensured that the table is completely included in the revised submission.

There is a supplemental figure that doesn't seem to be referenced in the text.

The supplemental figure (Fig. S1 of the original manuscript) is referenced in the text, but it may have been overlooked. To improve clarity, we have expanded the description in the manuscript so that the supplemental figure is more clearly referenced (Line 285‒291).

(3) Materials and Methods:

No power analysis was performed to calculate sample group sizes. The authors have used these experimental techniques in the past and could have easily used past data to inform these calculations.

We thank the reviewer for this important comment. We did not include a power analysis in the manuscript because this was the first time we compared Shh and other gene expression levels among ALM blastemas of different positional origins using RT-qPCR in our experimental system. As we did not have prior knowledge of the expected variability under these specific conditions, it was difficult to predetermine appropriate sample sizes.

Reviewer #3 (Recommendations for the authors):

General:

Congratulations - I found this an elegant and easy-to-read study with significant implications for the field! If possible, I would urge you to consider adding some more characterisation of Wnt10b and Fgf2- which cell types are they expressed in? If you can link your mechanisms to normal limb regeneration too (i.e., regenerating blastema, not ALM), this would significantly elevate the interest in your study.

We sincerely thank the reviewer for these encouraging comments. As also noted in our response to the editor’s comment, we have analyzed the expression patterns of Wnt10b and Fgf2 in regular blastemas (Line 294‒306). Although clear specific expression patterns along dorsoventral axis were not detected by ISH, likely due to technical limitations of sensitivity, RT-qPCR revealed significantly higher expression levels of Wnt10b in the dorsal half and Fgf2 in the ventral half of a regular blastema (Fig. S5). In addition, we analyzed published single-cell RNA-seq data (7 dpa blastema, Li et al., 2021) (Line 307‒321). As a result, Fgf2 expression was observed in the mesenchymal clusters, whereasWnt10b expression was observed in both mesenchymal and epithelial clusters (Fig. S6). However, because only a small fraction of cells expressed Wnt10b, the principal cellular source of WNT10B protein remains unclear. Therefore, defining the precise spatial patterns of Wnt10b and Fgf2 in regular regeneration will be an important goal for future work.

Data availability:

I assume that the RNA-sequencing data will be deposited at a public repository.

RNA-seq FASTQ files have been deposited in the DNA Data Bank of Japan (DDBJ; https://www.ddbj.nig.ac.jp/) under BioProject accession PRJDB38065. We have added a Data availability section to the revised manuscript.

References

Castilla-Ibeas, A., Zdral, S., Oberg, K. C., & Ros, M. A. (2024). The limb dorsoventral axis: Lmx1b’s role in development, pathology, evolution, and regeneration. Developmental Dynamics, 253(9), 798–814. https://doi.org/10.1002/dvdy.695

Johnson, G. L., Glasser, M. B., Charles, J. F., Duryea, J., & Lehoczky, J. A. (2022). En1 and Lmx1b do not recapitulate embryonic dorsal-ventral limb patterning functions during mouse digit tip regeneration. Cell Reports, 41(8), 111701. https://doi.org/10.1016/j.celrep.2022.111701

Stocum, D. (2017). Mechanisms of urodele limb regeneration. Regeneration, 4. https://doi.org/10.1002/reg2.92

Tank, P. W., & Holder, N. (1978). The effect of healing time on the proximodistal organization of double-half forelimb regenerates in the axolotl, Ambystoma mexicanum. Developmental Biology, 66(1), 72–85. https://doi.org/10.1016/0012-1606(78)90274-9

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Because the "source" and "target" tasks are merely parameter variations of the same paradigm, it is unclear whether EIDT achieves true crosstask transfer. The manuscript provides no measure of how consistent each participant's behaviour is across these variants (e.g., two- vs threestep MDP; easy vs difficult MNIST). Without this measure, the transfer results are hard to interpret. In fact, Figure 5 shows a notable drop in accuracy when transferring between the easy and difficult MNIST conditions, compared to transfers between accuracy-focused and speedfocused conditions. Does this discrepancy simply reflect larger withinparticipant behavioural differences between the easy and difficult settings? A direct analysis of intra-individual similarity for each task pair and how that similarity is related to EIDT's transfer performance is needed.

Thank you for your insightful comment. We agree that the tasks used in our study are variations of the same paradigm. Accordingly, we have revised the manuscript to consistently frame our findings as demonstrating individuality transfer "across task conditions" rather than "across distinct tasks."

In response to your suggestion, we have conducted a new analysis to directly investigate the relationship between individual behavioural patterns and transfer performance. As show in the new Figures 4, 11, S8, and S9, we found a clear relationship between the distance in the space of individual latent representation (called individuality index in the previous manuscript) and prediction performance. Specifically, prediction accuracy for a given individual's behaviour degrades as the latent representation of the model's source individual becomes more distant. This result directly demonstrates that our framework captures meaningful individual differences that are predictive of transfer performance across conditions.

We have also expanded the Discussion (Lines 332--343) to address the potential for applying this framework to more structurally distinct tasks, hypothesizing that this would rely on shared underlying cognitive functions.

Related to the previous comment, the individuality index is central to the framework, yet remains hard to interpret. It shows much greater within-participant variability in the MNIST experiment (Figure S1) than in the MDP experiment (Figure 3). Is such a difference meaningful? It is hard to know whether it reflects noisier data, greater behavioural flexibility, or limitations of the model.

Thank you for raising this important point about interpretability. To enhance the interpretability of the individual latent representation, we have added a new analysis for the MDP task (see Figures 6 and S4). By applying our trained encoder to data from simulated Q-learning agents with known parameters, we demonstrate that the dimensions of the latent space systematically map onto the agents' underlying cognitive parameters (learning rate and inverse temperature). This analysis provides a clearer interpretation by linking our model's data-driven representation to established theoretical constructs.

Regarding the greater within-participant variability observed in the MNIST task (visualized now in Figure S7), this could be attributed to several factors, such as greater behavioural flexibility in the perceptual task. However, disentangling these potential factors is complex and falls outside the primary scope of the current study, which prioritizes demonstrating robust prediction accuracy across different task conditions.

The authors suggests that the model's ability to generalize to new participants "likely relies on the fact that individuality indices form clusters and individuals similar to new participants exist in the training participant pool". It would be helpful to directly test this hypothesis by quantifying the similarity (or distance) of each test participant's individuality index to the individuals or identified clusters within the training set, and assessing whether greater similarity (or closer proximity) to the clusters in the training set is associated with higher prediction accuracy for those individuals in the test set.

Thank you for this excellent suggestion. We have performed the analysis you proposed to directly test this hypothesis. Our new results, presented in Figures 4, 11, S5, S8, and S9, quantify the distance between the latent representation of a test participant and that of the source participant used to generate the prediction model.

The results show a significant negative correlation: prediction accuracy consistently decreases as the distance in the latent space increases. This confirms that generalization performance is directly tied to the similarity of behavioural patterns as captured by our latent representation, strongly supporting our hypothesis.

Reviewer #2 (Public review):

The MNIST SX baseline appears weak. RTNet isn't directly comparable in structure or training. A stronger baseline would involve training the GRU directly on the task without using the individuality index-e.g., by fixing the decoder head. This would provide a clearer picture of what the index contributes.

We agree that a more direct baseline is crucial for evaluating the contribution of our transfer mechanism. For the Within-Condition Prediction scenario, the comparison with RTNet was intended only to validate that our task solver architecture could achieve average humanlevel task performance (Figure 7).

For the critical Cross-Condition Transfer scenario, we have now implemented a stronger and more appropriate baseline, which we call ``task solver (source).'' This model has the same architecture as our EIDT task solver but is trained directly on the source task data of the specific test participant. As shown in revised Figure 9, our EIDT framework significantly outperforms this direct-training approach, clearly demonstrating the benefit of the individuality transfer mechanism.

Although the focus is on prediction, the framework could offer more insight into how behaviour in one task generalizes to another. For example, simulating predicted behaviours while varying the individuality index might help reveal what behavioural traits it encodes.

Thank you for this valuable suggestion. To provide more insight into the encoded behavioural traits, we have conducted a new analysis linking the individual latent representation to a theoretical cognitive model. As detailed in the revised manuscript (Figures 6 and S4), we applied our encoder to simulated data from Q-learning agents with varying parameters. The results show a systematic relationship between the latent space coordinates and the agents' learning rates and inverse temperatures, providing a clearer interpretation of what the representation captures.

It's not clear whether the model can reproduce human behaviour when acting on-policy. Simulating behaviour using the trained task solver and comparing it with actual participant data would help assess how well the model captures individual decision tendencies.

We have added the suggested on-policy evaluation (Lines 195--207). In the revised manuscript (Figure 5), we present results from simulations where the trained task solvers performed the MDP task. We compared their performance (total reward and rate of the highly-rewarding action selected) against their corresponding human participants. The strong correlations observed demonstrate that our model successfully captures and reproduces individual-specific behavioural tendencies in an onpolicy setting.

Figures 3 and S1 aim to show that individuality indices from the same participant are closer together than those from different participants. However, this isn't fully convincing from the visualizations alone. Including a quantitative presentation would help support the claim.

We agree that the original visualizations of inter- and intraparticipant distances was not sufficiently convincing. We have therefore removed that analysis. In its place, we have introduced a more direct and quantitative analysis that explicitly links the individual latent representation to prediction performance (see Figures 4, 11, S5, S8, and S9). This new analysis demonstrates that prediction error for an individual is a function of distance in the latent space, providing stronger evidence that the representation captures meaningful, individual-specific information.

The transfer scenarios are often between very similar task conditions (e.g., different versions of MNIST or two-step vs three-step MDP). This limits the strength of the generalization claims. In particular, the effects in the MNIST experiment appear relatively modest, and the transfer is between experimental conditions within the same perceptual task. To better support the idea of generalizing behavioural traits across tasks, it would be valuable to include transfers across more structurally distinct tasks.

We agree with this limitation and have revised the manuscript to be more precise. We now frame our contribution as "individuality transfer across task conditions" rather than "across tasks" to accurately reflect the scope of our experiments. We have also expanded the Discussion section (Line 332-343) to address the potential and challenges of applying this framework to more structurally distinct tasks, noting that it would likely depend on shared underlying cognitive functions.

For both experiments, it would help to show basic summaries of participants' behavioural performance. For example, in the MDP task, first-stage choice proportions based on transition types are commonly reported. These kinds of benchmarks provide useful context.

We have added behavioral performance summaries as requested. For the MDP task, Figure 5 now compares the total reward and rate of highlyrewarding action selected between humans and our model. For the MNIST task, Figure 7 shows the rate of correct responses for humans, RTNet, and our task solver across all conditions. These additions provide better context for the model's performance.

For the MDP task, consider reporting the number or proportion of correct choices in addition to negative log-likelihood. This would make the results more interpretable.

Thank you for the suggestion. To make the results more interpretable, we have added a new prediction performance metric: the rate for behaviour matched. This metric measures the proportion of trials where the model's predicted action matches the human's actual choice. This is now included alongside the negative log-likelihood in Figures 2, 3, 4, 8, 9, and 11.

In Figure 5, what is the difference between the "% correct" and "% match to behaviour"? If so, it would help to clarify the distinction in the text or figure captions.

We have clarified these terms in the revised manuscript. As defined in the Result section (Lines 116--122, 231), "%correct" (now "rate of correct responses") is a measure of task performance, whereas "%match to behaviour" (now "rate for behaviour matched") is a measure of prediction accuracy.

For the cognitive model, it would be useful to report the fitted parameters (e.g., learning rate, inverse temperature) per individual. This can offer insight into what kinds of behavioural variability the individual latent representation might be capturing.

We have added histograms of the fitted Q-learning parameters for the human participants in Supplementary Materials (Figure S1). This analysis revealed which parameters varied most across the population and directly informed the design of our subsequent simulation study with Q-learning agents (see response to Comment 2-2), where we linked these parameters to the individual latent representation (Lines 208--223).

A few of the terms and labels in the paper could be made more intuitive. For example, the name "individuality index" might give the impression of a scalar value rather than a latent vector, and the labels "SX" and "SY" are somewhat arbitrary. You might consider whether clearer or more descriptive alternatives would help readers follow the paper more easily.

We have adopted the suggested changes for clarity.

"Individuality index" has been changed to "individual latent representation".

"Situation SX" and "Situation SY" have been renamed to the more descriptive "Within-Condition Prediction" and "Cross-Condition Transfer", respectively.

We have also added a table in Figure 7 to clarify the MNIST condition acronyms (EA/ES/DA/DS).

Please consider including training and validation curves for your models. These would help readers assess convergence, overfitting, and general training stability, especially given the complexity of the encoder-decoder architecture.

Training and validation curves for both the MDP and MNIST tasks have been added to Supplementary Materials (Figure S2 and S6) to show model convergence and stability.

Reviewer #3 (Public review):

To demonstrate the effectiveness of the approach, the authors compare a Q-learning cognitive model (for the MDP task) and RTNet (for the MNIST task) against the proposed framework. However, as I understand it, neither the cognitive model nor RTNet is designed to fit or account for individual variability. If that is the case, it is unclear why these models serve as appropriate baselines. Isn't it expected that a model explicitly fitted to individual data would outperform models that do not? If so, does the observed superiority of the proposed framework simply reflect the unsurprising benefit of fitting individual variability? I think the authors should either clarify why these models constitute fair control or validate the proposed approach against stronger and more appropriate baselines.

Thank you for raising this critical point. We wish to clarify the nature of our baselines:

For the MDP task, the cognitive model baseline was indeed designed to account for individual variability. We estimated its parameters (e.g., learning rate) from each individual's source task behaviour and then used those specific parameters to predict their behaviour in the target task. This makes it a direct, parameter-based transfer model and thus a fair and appropriate baseline for individuality transfer.

For the MNIST task, we agree that the RTNet baseline was insufficient for evaluating individual-level transfer in the "Cross-Condition Transfer" scenario. We have now introduced a much stronger baseline, the "task solver (source)," which is trained specifically on the source task data of each test participant. Our results (Figure 9) show that the EIDT framework significantly outperforms this more appropriate, individualized baseline, highlighting the value of our transfer method over direct, within-condition fitting.

It's not very clear in the results section what it means by having a shorter within-individual distance than between-individual distances. Related to the comment above, is there any control analysis performed for this? Also, this analysis appears to have nothing to do with predicting individual behavior. Is this evidence toward successfully parameterizing individual differences? Could this be task-dependent, especially since the transfer is evaluated on exceedingly similar tasks in both experiments? I think a bit more discussion of the motivation and implications of these results will help the reader in making sense of this analysis.

We agree that the previous analysis on inter- and intra-participant distances was not sufficiently clear or directly linked to the model's predictive power. We have removed this analysis from the manuscript. In its place, we have introduced a new, more direct analysis (Figures 4, 11, S5, S8, and S9) that demonstrates a quantitative relationship between the distance in the latent space and prediction accuracy. This new analysis shows that prediction error for an individual increases as a function of this distance, providing much stronger and clearer evidence that our framework successfully parameterizes meaningful individual differences.

The authors have to better define what exactly he meant by transferring across different "tasks" and testing the framework in "more distinctive tasks". All presented evidence, taken at face value, demonstrated transferring across different "conditions" of the same task within the same experiment. It is unclear to me how generalizable the framework will be when applied to different tasks.

Conceptually, it is also unclear to me how plausible it is that the framework could generalize across tasks spanning multiple cognitive domains (if that's what is meant by more distinctive). For instance, how can an individual's task performance on a Posner task predict task performance on the Cambridge face memory test? Which part of the framework could have enabled such a cross-domain prediction of task performance? I think these have to be at least discussed to some extent, since without it the future direction is meaningless.

We agree with your assessment and have corrected our terminology throughout the manuscript. We now consistently refer to the transfer as being "across task conditions" to accurately describe the scope of our findings.

We have also expanded our Discussion (Line 332-343) to address the important conceptual point about cross-domain transfer. We hypothesize that such transfer would be possible if the tasks, even if structurally different, rely on partially shared underlying cognitive functions (e.g., working memory). In such a scenario, the individual latent representation would capture an individual's specific characteristics related to that shared function, enabling transfer. Conversely, we state that transfer between tasks with no shared cognitive basis would not be expected to succeed with our current framework.

How is the negative log-likelihood, which seems to be the main metric for comparison, computed? Is this based on trial-by-trial response prediction or probability of responses, as what usually performed in cognitive modelling?

The negative log-likelihood is computed on a trial-by-trial basis. It is based on the probability the model assigned to the specific action that the human participant actually took on that trial. This calculation is applied consistently across all models (cognitive models, RTNet, and EIDT). We have added sentences to the Results section to clarify this point (Lines 116--122).

None of the presented evidence is cross-validated. The authors should consider performing K-fold cross-validation on the train, test, and evaluation split of subjects to ensure robustness of the findings.

All prediction performance results reported in the revised manuscript are now based on a rigorous leave-one-participant-out cross-validation procedure to ensure the robustness of our findings. We have updated the

Methods section to reflect this (Lines 127--129 and 229).

For some purely illustrative visualizations (e.g., plotting the entire latent space in Figures S3 and S7), we used a model trained on all participants' data to provide a single, representative example and avoid clutter. We have explicitly noted this in the relevant figure captions.

The authors excluded 25 subjects (20% of the data) for different reasons. This is a substantial proportion, especially by the standards of what is typically observed in behavioral experiments. The authors should provide a clear justification for these exclusion criteria and, if possible, cite relevant studies that support the use of such stringent thresholds.

We acknowledge the concern regarding the exclusion rate. The previous criteria were indeed empirical. We have now implemented more systematic exclusion procedure based on the interquartile range of performance metrics, which is detailed in Section 4.2.2 (Lines 489--498). This revised, objective criterion resulted in the exclusion of 42 participants (34% of the initial sample). While this rate is high, we attribute it to the online nature of the data collection, where participant engagement can be more variable. We believe applying these strict criteria was necessary to ensure the quality and reliability of the behavioural data used for modeling.

The authors should do a better job of creating the figures and writing the figure captions. It is unclear which specific claim the authors are addressing with the figure. For example, what is the key message of Figure 2C regarding transfer within and across participants? Why are the stats presentation different between the Cognitive model and the EIDT framework plots? In Figure 3, it's unclear what these dots and clusters represent and how they support the authors' claim that the same individual forms clusters. And isn't this experiment have 98 subjects after exclusion, this plot has way less than 98 dots as far as I can tell. Furthermore, I find Figure 5 particularly confusing, as the underlying claim it is meant to illustrate is unclear. Clearer figures and more informative captions are needed to guide the reader effectively.

We agree that several figures and analyses in the original manuscript were unclear, and we have thoroughly revised our figures and their captions to improve clarity.

The confusing analysis in the old Figures 2C and 5 (Original/Others comparison) have been completely removed. The unclear visualization of the latent space for the test pool (old Figure 3 showing representations only from test participants) has also been removed to avoid confusion. For visualization of the overall latent space, we now use models trained on all data (Figures S3 and S7) and have clarified this in the captions. In place of these removed analyses, we have introduced a new, more intuitive "cross-individual" analysis (presented in Figures 4, 11, S5, S8, and S9). As explained in the new, more detailed captions, this analysis directly plots prediction performance as a function of the distance in latent space, providing a much clearer demonstration of how the latent representation relates to predictive accuracy.

I also find the writing somewhat difficult to follow. The subheadings are confusing, and it's often unclear which specific claim the authors are addressing. The presentation of results feels disorganized, making it hard to trace the evidence supporting each claim. Also, the excessive use of acronyms (e.g., SX, SY, CG, EA, ES, DA, DS) makes the text harder to parse. I recommend restructuring the results section to be clearer and significantly reducing the use of unnecessary acronyms.

Thank you for this feedback. We have made significant revisions to improve the clarity and organization of the manuscript. We have renamed confusing acronyms: "Situation SX" is now "Within- Condition Prediction," and "Situation SY" is now "Cross-Condition Transfer." We also added a table to clarify the MNIST condition acronyms (EA/ES/DA/DS) in Figure 7.

The Results section has been substantially restructured with clearer subheadings.

Author response:

Reviewer #1

(1) Mechanistic insight into how Hsp70 but not Hsc70 increase PL-SF FL tau aggregation/pathology is missing. This is despite both chaperones binding to PL-SF FL tau. What species of tau does Hsp70 bind, and what cofactors are important in this process?

We agree that explaining why Hsp70, but not Hsc70, promotes tau aggregation would strengthen the study. Although both chaperones bind tau, they diverge slightly in 1) protein sequence, 2) biochemical activity, and 3) co-chaperone engagement.

Sequence: Hsp70 has an extra cysteine residue (Cys306) that is highly reactive to oxidation and a glycine residue that is critical for cysteine oxidation (Gly557). Both residues are specific to Hsp70 (not present in Hsc70) and may alter Hsp70 conformation or client handling (Hong et al., 2022).

Biochemical activity: Prior studies indicate that Hsp70’s ATPase domain (NBD) is critical for tau interactions (Jinwal et al., 2009; Fontaine et al., 2015; Young et al., 2016) and can be disrupted with point mutations including K71E and E175S for ATPase and A406G/V438G for substrate binding (Fontaine et al., 2015).

Co-chaperone engagement: Hsp70 recruits the co-chaperone and E3 ubiquitin ligase CHIP/Stub1 more strongly than Hsc70, suggesting co-chaperone engagement could lead to differences in tau processing (Jinwal et al., 2013).

To directly test how the two closely related chaperones could differentially impact tau, we plan to perform the following experiments:

(a) We will mutate residues responsible for cysteine reactivity in Hsp70 including the cysteine itself (Cys306) and the critical glycine that facilitates cysteine reactivity (Gly557). These residues will be deleted from Hsp70 or alternatively inserted into Hsc70 to determine whether cysteine reactivity is the reason for Hsp70’s ability to drive tau aggregation.

(b) We will generate Hsp70 mutants lacking ATPase- or substrate-binding mutants to determine which Hsp70 domains are responsible for driving tau aggregation.

(c) We will perform seeding assays in stable tau-expressing cell lines to determine whether Hsp70/Hsc70 overexpression or depletion alters seeded tau aggregation.

(d) We will perform confocal microscopy to determine the extent of co-localization of Hsp70 or Hsc70 with phospho-tau, oligomeric tau, or Thioflavin-S (ThioS) to identify which tau species are engaged by Hsp70/Hsc70.

(e) We will perform immunoprecipitation pull-downs followed by mass spectrometry to globally identify any relevant Hsp70/Hsc70 interacting factors that might account for the differences in tau aggregation.

(2) The study relies heavily on densitometry of bands to draw conclusions; in several instances, the blots are overexposed to accurately quantify the signal.

All immunoblots were acquired as 16-bit TIFFs with exposure settings chosen to prevent pixel saturation, and quantification was performed on raw, unsaturated images. Brightness and contrast adjustments were applied only for visualization and did not alter pixel values used for analysis. All quantified bands fell within the linear range of the detector, with one exception in Figure 7B, which we removed from quantification. We will add both low- and high-exposure versions of immunoblots to the revised figures to demonstrate signal linearity and dynamic range.

Reviewer #2

(1) Although the PL-SF model can accelerate tau aggregation, it is crucial to determine whether this aligns with the temporal progression and spatial distribution of tau pathology in the brains of patients with tauopathies.

No single tauopathy model fully recapitulates the temporal and spatial progression of human tauopathies. The PL-SF system is not intended to model the disease course. Rather, it is an excellent model for mechanistic studies of mature tau aggregation, which is otherwise challenging to study. We note that prior studies showed that PL-SF tau expression in transgenic mice (Xia et al., 2022 and Smith et al., 2025) and rhesus monkeys (Beckman et al., 2021) led to prion-like tau seeding and aggregation in hippocampal and cortical regions. Indeed, the spatial and temporal tau aggregation patterns aligned with features of human tauopathies. So far, these findings all support PL-SF as a valid accelerated model of tauopathy than can be used to interrogate pathogenic mechanisms that impact tau processing, degradation, and/or aggregation.

(2) The authors did not elucidate the specific molecular mechanism by which Hsp70 promotes tau aggregation.

We agree that a deeper understanding of the molecular mechanism is needed. The revision experiments outlined above (Reviewer #1, point #1) will define how Hsp70 promotes tau aggregation by testing sequence contributions, dissecting ATPase and substrate-binding domain requirements, and mapping Hsp70/Hsc70 interactors to directly address this mechanistic question.

(3) Some figures in this study show large error bars in the quantitative data (some statistical analysis figures, MEA recordings, etc.), indicating significant inter-sample variability. It is recommended to label individual data points in all quantitative figures and clearly indicate them in figure legends.

We acknowledge the inter-sample variability in some of the quantitative datasets. This level of variability can occur in primary neuronal cultures (e.g., MEA recordings) that are sensitive to growth and surface adhesion conditions, leading to many technical considerations. To improve transparency and interpretation, we will revise all quantitative figures to display individual data points overlaid on summary statistics and will update figure legends to clearly indicate sample sizes and statistical tests used.

References

Hong Z, Gong W, Yang J, Li S, Liu Z, Perrett S, Zhang H. Exploration of the cysteine reactivity of human inducible Hsp70 and cognate Hsc70. J Biol Chem. 2023 Jan;299(1):102723. doi: 10.1016/j.jbc.2022.102723. Epub 2022 Nov 19. PMID: 36410435; PMCID: PMC9800336.

Jinwal UK, Miyata Y, Koren J 3rd, Jones JR, Trotter JH, Chang L, O'Leary J, Morgan D, Lee DC, Shults CL, Rousaki A, Weeber EJ, Zuiderweg ER, Gestwicki JE, Dickey CA. Chemical manipulation of hsp70 ATPase activity regulates tau stability. J Neurosci. 2009 Sep 30;29(39):12079-88. doi: 10.1523/JNEUROSCI.3345-09.2009. PMID: 19793966; PMCID: PMC2775811.

Fontaine SN, Rauch JN, Nordhues BA, Assimon VA, Stothert AR, Jinwal UK, Sabbagh JJ, Chang L, Stevens SM Jr, Zuiderweg ER, Gestwicki JE, Dickey CA. Isoform-selective Genetic Inhibition of Constitutive Cytosolic Hsp70 Activity Promotes Client Tau Degradation Using an Altered Co-chaperone Complement. J Biol Chem. 2015 May 22;290(21):13115-27. doi: 10.1074/jbc.M115.637595. Epub 2015 Apr 11. PMID: 25864199; PMCID: PMC4505567

Young ZT, Rauch JN, Assimon VA, Jinwal UK, Ahn M, Li X, Dunyak BM, Ahmad A, Carlson G, Srinivasan SR, Zuiderweg ERP, Dickey CA, Gestwicki JE. Stabilizing the Hsp70‑Tau Complex Promotes Turnover in Models of Tauopathy. Cell Chem Biol. 2016 Aug 4;23(8):992–1001. doi:10.1016/j.chembiol.2016.04.014.

Jinwal UK, Akoury E, Abisambra JF, O'Leary JC 3rd, Thompson AD, Blair LJ, Jin Y, Bacon J, Nordhues BA, Cockman M, Zhang J, Li P, Zhang B, Borysov S, Uversky VN, Biernat J, Mandelkow E, Gestwicki JE, Zweckstetter M, Dickey CA. Imbalance of Hsp70 family variants fosters tau accumulation. FASEB J. 2013 Apr;27(4):1450-9. doi: 10.1096/fj.12-220889. Epub 2012 Dec 27. PMID: 23271055; PMCID: PMC3606536.

Xia, Y., Prokop, S., Bell, B.M. et al. Pathogenic tau recruits wild-type tau into brain inclusions and induces gut degeneration in transgenic SPAM mice. Commun Biol 5, 446 (2022). https://doi.org/10.1038/s42003-022-03373-1.

Smith ED, Paterno G, Bell BM, Gorion KM, Prokop S, Giasson BI. Tau from SPAM Transgenic Mice Exhibit Potent Strain-Specific Prion-Like Seeding Properties Characteristic of Human Neurodegenerative Diseases. Neuromolecular Med. 2025 May 30;27(1):44. doi: 10.1007/s12017-025-08850-4. PMID: 40447946; PMCID: PMC12125038.

Beckman D, Chakrabarty P, Ott S, Dao A, Zhou E, Janssen WG, Donis-Cox K, Muller S, Kordower JH, Morrison JH. A novel tau-based rhesus monkey model of Alzheimer's pathogenesis. Alzheimers Dement. 2021 Jun;17(6):933-945. doi: 10.1002/alz.12318. Epub 2021 Mar 18. PMID: 33734581; PMCID: PMC8252011.

Author response:

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

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

This study presents convincing findings that oligodendrocytes play a regulatory role in spontaneous neural activity synchronisation during early postnatal development, with implications for adult brain function. Utilising targeted genetic approaches, the authors demonstrate how oligodendrocyte depletion impacts Purkinje cell activity and behaviours dependent on cerebellar function. Delayed myelination during critical developmental windows is linked to persistent alterations in neural circuit function, underscoring the lasting impact of oligodendrocyte activity. 

Strengths: 

(1) The research leverages the anatomically distinct olivocerebellar circuit, a well-characterized system with known developmental timelines and inputs, strengthening the link between oligodendrocyte function and neural synchronization. 

(2) Functional assessments, supported by behavioral tests, validate the findings of in vivo calcium imaging, enhancing the study's credibility. 

(3) Extending the study to assess the long-term effects of early-life myelination disruptions adds depth to the implications for both circuit function and behavior.

We appreciate these positive evaluation.

Weaknesses: 

(1) The study would benefit from a closer analysis of myelination during the periods when synchrony is recorded. Direct correlations between myelination and synchronized activity would substantiate the mechanistic link and clarify if observed behavioral deficits stem from altered myelination timing. 

We appreciate the reviewer’s thoughtful suggestion and have expanded the manuscript to clarify how oligodendrocyte maturation relates to the development of Purkinje-cell synchrony. The developmental trajectory of Purkinje-cell synchrony has already been comprehensively characterized by Good et al. (2017, Cell Reports 21: 2066–2073): synchrony drops from a high level at P3–P5 to adult-like values by P8. We found that the myelination in the cerebellum starts to appear from P5-P7 (Figure S1A, B), indicating that the timing of Purkinje cell desynchronization coincides with the initial appearance of oligodendrocytes and myelin in the cerebellum. To determine whether myelin growth could nevertheless modulate this process, we quantified ASPA-positive oligodendrocyte density and MBP-positive bundle thickness and area at P10, P14, P21 and adulthood (Fig. 1J, K, Fig. S1E). Both metrics increase monotonically and clearly lag behind the rapid drop in synchrony, indicating that myelination could be not the primary trigger for the desynchronization. When oligodendrocytes were ablated during the second postnatal week, the synchrony was reduced (new Fig. 2). Thus, once myelination is underway, oligodendrocytes become critical for maintaining the synchrony, acting not as the initiators but as the stabilizers and refiners of the mature network state.

We have added the new subsection in discussion (lines 451–467) now in which we propose a two-phase model. Phase I (P3–P8): High early synchrony is generated by non-myelin mechanisms (e.g. transient gap junctions, shared climbing-fiber input). Phase II (P8-). As oligodendrocytes proliferate and ensheath axons, they fine-tune conduction velocity and stabilize the mature, low-synchrony network state.

We believe these additions fully address the reviewer’s concerns.

(2) Although the study focuses on Purkinje cells in the cerebellum, neural synchrony typically involves cross-regional interactions. Expanding the discussion on how localized Purkinje synchrony affects broader behaviors - such as anxiety, motor function, and sociality - would enhance the findings' functional significance.

We appreciate the reviewer’s helpful suggestion and have expanded the Discussion (lines 543–564) to clarify how localized Purkinje-cell synchrony can influence broader behavioral domains. In the revised text we note that changes in PC synchrony propagate  into thalamic, prefrontal, limbic, and parietal targets, thereby impacting distributed networks involved in motor coordination, affect, and social interaction. Our optogenetic rescue experiments further support this framework, as transient resynchronization of PCs normalized sociability and motor coordination while leaving anxiety-like behavior impaired. This dissociation highlights that different behavioral domains rely to varying degrees on precise cerebellar synchrony and underscores how even localized perturbations in Purkinje timing can acquire system-level significance.

(3) The authors discuss the possibility of oligodendrocyte-mediated synapse elimination as a possible mechanism behind their findings, drawing from relevant recent literature on oligodendrocyte precursor cells. However, there are no data presented supporting this assumption. The authors should explain why they think the mechanism behind their observation extends beyond the contribution of myelination or remove this point from the discussion entirely.

We thank the reviewer for pointing out that our original discussion of oligodendrocyte-mediated synapse elimination was not directly supported by data in the present manuscript. Because we are actively analyzing this question in a separate, follow-up study, we have deleted the speculative passage to keep the current paper focused on the demonstrated, myelination-dependent effects. We believe this change sharpens the mechanistic narrative and fully addresses the reviewer’s concern.

(4) It would be valuable to investigate the secondary effects of oligodendrocyte depletion on other glial cells, particularly astrocytes or microglia, which could influence long-term behavioral outcomes. Identifying whether the lasting effects stem from developmental oligodendrocyte function alone or also involve myelination could deepen the study's insights. 

We thank the reviewer for raising this point and have performed the requested analyses. Using IBA1 immunostaining for microglia and S100b for Bergmann glia, we quantified cell density and these marker signal intensity at P14 and P21. Neither microglial or Bergmann-glial differed between control and oligodendrocyte-ablated mice at either time‐point (new Figure S2). These results indicate that the behavioral phenotypes we report are unlikely to arise from secondary activation or loss of other glial populations.

We now added results (lines 275–286) and also discuss myelination and other oligodendrocyte function (lines 443–450). It remains difficult to disentangle conduction-related effects from myelination-independent trophic roles of oligodendrocytes. We therefore note explicitly that future work employing stage-specific genetic tools or acute metabolic manipulations will be required to parse these contributions more definitively.

(5) The authors should explore the use of different methods to disturb myelin production for a longer time, in order to further determine if the observed effects are transient or if they could have longer-lasting effects.

We agree that distinguishing transient from enduring effects is critical. Importantly, our original submission already included data demonstrating a persistent deficit of PC population synchrony (Fig. 4, previous Fig. 3): (i) at P14—the early age after oligodendrocyte ablation—population synchrony is reduced, and (ii) the same deficit is still present in adults (P60–P70) despite full recovery of ASPA-positive cell density and MBP-area and -thickness (Fig. 2H-K, Fig. S1E, and Fig. 4). We also performed the ablation of oligodendrocytes after the third postnatal week. Despite a similar acute drop in ASPA-positive cells, neither population synchrony nor anxiety-, motor-, or social behaviors differed from littermate controls. Thus, extending myelin disruption beyond the developmental window does not exacerbate or prolong the phenotype, whereas a short perturbation within that window leaves a permanent timing defect. These findings strengthen our conclusion that it is the developmental oligodendrocyte/myelination program itself—rather than ongoing adult myelin production—that is essential for establishing stable network synchrony. We now highlight this point explicitly in the revised Discussion (lines 507–522).

(6) Throughout the paper, there are concerns about statistical analyses, particularly on the use of the Mann-Whitney test or using fields of view as biological replicates.

We appreciate the reviewer’s guidance on appropriate statistical treatment. To address these concerns we have re-analyzed all datasets that contained multiple measurements per animal (e.g., fields of view, lobules, or trials) using nested statistics with animal as the higher-order unit. Specifically, we applied a two-level nested ANOVA when more than two groups were compared and a nested t-test when two conditions were present. The re-analysis confirmed all original conclusions. Because the nested models yielded comparable effect sizes to the Mann–Whitney tests, we have retained the mean ± SEM for ease of comparison with prior literature but now also report all values for each mouse in Table 1. In cases where a single measurement per mouse was compared between two groups, we used the Mann–Whitney test and present the results in the graphs as median values.

Major

(1) The authors present compelling evidence that early loss of myelination disrupts synchronous firing prematurely. However, synchronous neuronal firing does not equate to circuit synchronization. It is improbable that myelination directly generates synchronous firing in Purkinje cells (PCs). For instance, Foran et al. (1992) identified that cerebellar myelination begins around postnatal day 6 (P6), while Good et al. (2017) recorded a developmental decline in PC activity correlation from P5-P11. To clarify myelin's role, we recommend detailed myelin imaging through light microscopy (MBP staining at higher magnification) to assess the extent of myelin removal accurately. Myelin sheaths, as shown by Snaidero et al. (2020), can persist after oligodendrocyte (OL) death, particularly following DTA induction (Pohl et al. 2011). Quantification of MBP+ area, rather than mean MBP intensity, is necessary to accurately measure myelin coverage.

We appreciate the reviewer’s concern that residual sheaths might remain after oligodendrocyte ablation and have therefore re-examined myelin at higher spatial resolution. Then, two independent metrics were extracted: MBP⁺ area fraction in the white matter and MBP⁺ bundle thickness (new Figure 1J, K, and Fig. S1E). We confirm a robust, transient loss of myelin at P10 and P14 as shown by the reduction of MBP⁺ area and MBP⁺ bundle thickness. Both parameters recovered to control values by P21 and adulthood, indicating effective remyelination. These data demonstrate that, in our paradigm, oligodendrocyte ablation is accompanied by substantial sheath loss rather than the persistent myelin reported after acute toxin exposure. We have added them in Result (lines 266–271).

The results reinforce the view that myelin removal and/or loss of trophic support during a narrow developmental window drive the long-term hyposynchrony and behavioral phenotypes we report. We have added the new subsection in discussion (lines 443–450) now in which we propose a two-phase model. Phase I (P3–P8): High early synchrony is generated by non-myelin mechanisms (e.g. transient gap junctions, shared climbing-fiber input). Phase II (P8-). As oligodendrocytes proliferate and ensheath axons, they fine-tune conduction velocity and stabilize the mature, low-synchrony network state. We believe these additions fully address the reviewer’s concerns.

(2) Surprisingly, the authors speculate about oligodendrocyte-mediated synaptic pruning without supportive data, shifting the focus away from the potential impact of myelination. Even if OLs perform synaptic pruning, OL depletion would likely maintain synchrony, yet the opposite was observed. Further characterisation of the model and the potential source of the effect is needed. 

We thank the reviewer for pointing out that our original discussion of oligodendrocyte-mediated synapse elimination was not directly supported by data in the present manuscript. Because we are actively analyzing this question in a separate, follow-up study, we have deleted the speculative passage to keep the current paper focused on the demonstrated, myelination-dependent effects. We believe this change sharpens the mechanistic narrative and fully addresses the reviewer’s concern.

(3) Improved characterization of the DTA model would add clarity. Although almost all infected cells are reported as OLs, quantification of infected OL-lineage cells (e.g., via Olig2 staining) would verify this. It remains possible that observed activity changes are driven by OL-independent demyelination effects. We suggest cross-staining with Iba1 and GFAP to rule out inflammation or gliosis. 

We thank the reviewer for this important suggestion and have expanded our histological characterization accordingly. First, to verify that DTA expression is confined to mature oligodendrocytes, we co-stained cerebellar sections collected 7 days after AAV-hMAG-mCherry injection with Olig2 (pan-OL lineage) and ASPA (mature OL marker) as shown in Figure S1C-D. Quantitative analysis revealed that 100 % of mCherry⁺ cells were Olig2⁺/ASPA⁺, whereas mCherry signal was virtually absent in Olig2⁺/ASPA⁻ immature oligodendrocytes. These data confirm that our DTA manipulation targets mature myelinating OLs rather than earlier lineage stages. We have added them in Result (lines 260–262).

Second, to examine indirect effects mediated by other glia, we performed cross-staining with IBA1 (microglia) and S100β (Bergmann). Cell density and fluorescence intensity for each marker were indistinguishable between control and DTA groups at P14 and P21 (Figure S2A-H). Thus, neither inflammation nor astro-/microgliosis accompanies OL ablation. We have added them in Result (lines 275–286).

Collectively, these results demonstrate that the observed desynchronization and behavioral phenotypes arise from specific loss of mature oligodendrocytes and their myelin, rather than from off-target viral expression or secondary glial responses.

(4) The use of an independent model of myelin loss, such as the inducible Myrf knockout mouse with a MAG promoter, to assess if oligodendrocyte loss causes temporary or sustained impacts, employing an extended knockout model like Myrf cKO with MAG-Cre viral methods would be advantageous.

We agree that distinguishing transient from enduring effects is critical. Importantly, our original submission already included data demonstrating a persistent deficit of PC population synchrony (Fig. 4, previous Fig. 3): (i) at P13-15—the early age after oligodendrocyte ablation—population synchrony is reduced, and (ii) the same deficit is still present in adults (P60–P70) despite full recovery of ASPA-positive cell density and MBP-area and -thickness (Fig. 2H-K, Fig. S1E, and Fig. 4). We also performed the ablation of oligodendrocytes after the third postnatal week. Despite a similar acute drop in ASPA-positive cells, neither population synchrony nor anxiety-, motor-, or social behaviors differed from littermate controls. Thus, extending myelin disruption beyond the developmental window does not exacerbate or prolong the phenotype, whereas a short perturbation within that window leaves a permanent timing defect. These findings strengthen our conclusion that it is the developmental oligodendrocyte/myelination program itself—rather than ongoing adult myelin production—that is essential for establishing stable network synchrony. We now highlight this point explicitly in the revised Discussion (lines 507–522).

(5) For statistical robustness, the use of non-parametric tests (Mann-Whitney) necessitates reporting the median instead of the mean as the authors do. Furthermore, as repeated measurements within the same animal are not independent, the authors should ideally use nested ANOVA (or nested t-test comparing two conditions) to validate their findings (Aarts et al., Nat. Neuroscience 2014). Alternatively use one-way ANOVA with each animal as a biological replicate, although this means that the distribution in the data sets per animal is lost.

We appreciate the reviewer’s guidance on appropriate statistical treatment. To address these concerns we have re-analyzed all datasets that contained multiple measurements per animal (e.g., fields of view, lobules, or trials) using nested statistics with animal as the higher-order unit. Specifically, we applied a two-level nested ANOVA when more than two groups were compared and a nested t-test when two conditions were present. The re-analysis confirmed all original conclusions. Because the nested models yielded comparable effect sizes to the Mann–Whitney tests, we have retained the mean ± SEM for ease of comparison with prior literature but now also report all values for each mouse in Table 1. In cases where a single measurement per mouse was compared between two groups, we used the Mann–Whitney test and present the results in the graphs as median values.

Minor Points 

(1) In all figures, please specify the ages at which each procedure was conducted, as demonstrated in Figure 2A.

All main and supplementary figures now specify the exact postnatal age.

(2) Clarify the selection criteria for regions of interest (ROI) in calcium imaging, and provide representative ROIs.

We appreciate the reviewer’s guidance. We have clarified that our ROI detection followed the protocol reported by our previous paper (Tanigawa et al., 2024, Communications Biology) (lines 177-178) and representative Purkinje cell ROIs are now shown in Fig. 2B.

(3) Include data on the proportion of climbing fiber or inferior olive neurons expressing Kir and the total number of neurons transfected, which would help contextualize the observed effects on PC synchronization and its broader implications for cerebellar circuit function.

We appreciate the reviewer’s guidance. New Fig. 7C summarizes the efficiency of AAV-GFP and AAV-Kir2.1-GFP injections into the inferior olive. Across 4 mice PCs with GFP-labeled CFs was detected in 19.3 ± 11.9 (mean ± S.D.) % for control and 26.2 ± 11.8 (mean ± S.D.) % for Kir2.1 of PCs. These numbers are reported in the Results (lines 373–375).

(4) Higher magnification images in Figures 1 and S3 would improve visual clarity. 

We have addressed the request for higher-magnification images in two ways. First, all panels in Figure S3 were placed on a larger canvas. Second, in Figure 1 we adjusted panel sizes to emphasize fine structure: panel 1C already represents an enlargement of the RFP positive cells shown in 1B, and panel 1H and 1J now occupies a wider span so that every ASPA-positive cell body can be distinguished. Should the reviewer still require an even closer view, we have additional ready for upload.

(5) Consider language editing to enhance overall clarity and readability.

The entire manuscript was edited to improve flow, consistency, and readability.

(6) Refine the discussion to align with the presented data.

We have refined the discussion.

Thank you once again for your constructive suggestions and comments. We believe these changes have improved the clarity and readability of our manuscript.

Reviewer #2 (Public review):

We appreciate Reviewer #2’s positive evaluation of our work and thank him/her for the constructive suggestions and comments. We followed these suggestions and comments and have conducted additional experiments. We have rewritten the manuscript and revised the figures according to the points Reviewer #1 mentioned. Our point-by-point responses to the comments are as follows.

Summary:

In this manuscript, the authors use genetic tools to ablate oligodendrocytes in the cerebellum during postnatal development. They show that the oligodendrocyte numbers return to normal post-weaning. Yet, the loss of oligodendrocytes during development seems to result in decreased synchrony of calcium transients in Purkinje neurons across the cerebellum. Further, there were deficits in social behaviors and motor coordination. Finally, they suppress activity in a subset of climbing fibers to show that it results in similar phenotypes in the calcium signaling and behavioral assays. They conclude that the behavioral deficits in the oligodendrocyte ablation experiments must result from loss of synchrony. 

Strengths:

Use of genetic tools to induce perturbations in a spatiotemporally specific manner.

We appreciate these positive evaluation.

Weaknesses: 

The main weakness in this manuscript is the lack of a cohesive causal connection between the experimental manipulation performed and the phenotypes observed. Though they have taken great care to induce oligodendrocyte loss specifically in the cerebellum and at specific time windows, the subsequent experiments do not address specific questions regarding the effect of this manipulation.

Calcium transients in Purkinje neurons are caused to a large extent by climbing fibers, but there is evidence for simple spikes to also underlie the dF/F signatures (Ramirez and Stell, Cell Reports, 2016).

We thank the reviewer for drawing attention to the work of Ramirez & Stell (2016), which showed that simple-spike bursts can elicit Ca²⁺ rises, but only in the soma and proximal dendrites of adult Purkinje cells. In our study, Regions of Interest were restricted to the dendritic arbor, where SS-evoked signals are essentially undetectable (Ramirez & Stell, 2016), whereas climbing-fiber complex spikes generate large, all-or-none transients (Good et al., 2017). Accordingly, even if a rare SS-driven event reached threshold it would likely fall outside our ROIs.

In addition, we directly imaged CF population activity by expressing GCaMP7f in inferior-olive neurons. Correlation analysis of CF boutons revealed that DTA ablation lowers CF–CF synchrony at P14 (new Fig. 3A–D). Because CF synchrony is a principal driver of Purkinje-cell co-activation, this reduction provides a mechanistic link between oligodendrocyte loss and the hyposynchrony we observe among Purkinje cells. Consistent with this interpretation, electrophysiological recordings showed that parallel-fiber EPSCs and inhibitory synaptic inputs onto Purkinje cells were unchanged by DTA treatment (Fig. 3E-H) , which makes it less likely that the reduced synchrony simply reflects changes in other excitatory or inhibitory synaptic drive.

That said, SS-dependent somatic Ca²⁺ signals could still influence downstream plasticity and long-term cerebellar function. In future work we therefore plan to combine somatic imaging with stage-specific oligodendrocyte manipulations to test whether SS-evoked Ca²⁺ dynamics are themselves modulated by oligodendrocyte support. We have added these descriptions in the Results (lines 288–294) and Discussion (lines 423–434).

Also, it is erroneous to categorize these calcium signals as signatures of "spontaneous activity" of Purkinje neurons as they can have dual origins.

Thank you for pointing out the potential ambiguity. In the revised manuscript we have clarified how we use the term “spontaneous activity” in the context of our measurements (lines 289-290). Our calcium imaging was restricted to the dendritic arbor of Purkinje cells, where calcium transients are dominated by climbing-fiber (CF) inputs (Ramirez & Stell, 2016; Good et al., 2017). Thus, the synchrony values reported here primarily reflect CF-driven complex spikes rather than mixed signals of dual origin. We have revised the Results section accordingly (lines 289–293) to make this measurement-specific limitation explicit.

Further, the effect of developmental oligodendrocyte ablation on the cerebellum has been previously reported by Mathis et al., Development, 2003. They report very severe effects such as the loss of molecular layer interneurons, stunted Purkinje neuron dendritic arbors, abnormal foliations, etc. In this context, it is hardly surprising that one would observe a reduction of synchrony in Purkinje neurons (perhaps due to loss of synaptic contacts, not only from CFs but also from granule cells).

We appreciate the reviewer’s comparison to Mathis et al. (2003). Mathis et al. used MBP–HSV-TK transgenic mice in which systemic FIAU treatment eliminates oligodendrocytes. When ablation began at P1, they observed severe dysmorphology—loss of molecular-layer interneurons, Purkinje-cell (PC) dendritic stunting, and abnormal foliation. Crucially, however, the same study reports that starting the ablation later (FIAU from P6-P20) left cerebellar cyto-architecture entirely normal.

Our AAV MAG-DTA paradigm resembles this later window. Our temporally restricted DTA protocol produces the same ‘late-onset’ profile—robust yet reversible hypomyelination with no loss of Purkinje cells, interneurons, dendritic length, or synaptic input (new Fig. S1–S2, Fig. 3E-H). The enduring hyposynchrony we report therefore cannot be attributed to the dramatic anatomical defects seen after prenatal ablation, but instead reveals a specific requirement for early-postnatal myelin in stabilizing PC synchrony, especially affecting CF-CF synchrony.

This clarification shows that we have carefully considered the Mathis model and that our findings not only replicate, but also extend the earlier work. We have added these description in Result (lines 273-286)

The last experiment with the expression of Kir2.1 in the inferior olive is hardly convincing.

We appreciate the reviewer’s concern and have reinforced the causal link between Purkinje-cell synchrony and behavior. To test whether restoring PC synchrony is sufficient to rescue behavior, we introduced a red-shifted opsin (AAV-L7-rsChrimine) into PCs of DTA mice raised to adulthood. During testing we delivered 590-nm light pulses (10 ms, 1 Hz) to the vermis, driving brief, population-wide spiking (new Fig. 8). This periodic re-synchronization left anxiety measures unchanged (open-field center time remained low) but rescued both motor coordination (rotarod latency normalized to control levels) and sociability (time spent with a novel mouse restored). The dissociation implies that distinct behavioral domains differ in their sensitivity to PC timing precision and confirms that reduced synchrony—not cell loss or gross circuit damage (Fig. S1F, S2)—is the primary driver of the motor and social deficits. Together, the optogenetic rescue establishes a bidirectional, mechanistic link between PC synchrony and behavior, addressing the reviewer’s reservations about the original experiment. We have added these descriptions in Result (lines 394-415)

In summary, while the authors used a specific tool to probe the role of developmental oligodendrocytes in cerebellar physiology and function, they failed to answer specific questions regarding this role, which they could have done with more fine-grained experimental analysis.

Thank you once again for your constructive suggestions and comments. We believe these changes have improved the clarity and readability of our manuscript.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Show that ODC loss is specific to the cerebellum.

We thank the reviewer for requesting additional evidence. To verify that oligodendrocyte ablation was confined to the cerebellum, we injected an AAV carrying mCherry under the human MAG promoter (AAV-hMAG-mCherry) into the cerebellum, and screened the whole brain one week later. As shown in the new Figure 1E–G, mCherry positive cells were present throughout the injected cerebellar cortex (Fig. 1E), but no fluorescent cells were detected in extracerebellar regions—including cerebral cortex, medulla, pons, midbrain. These data demonstrate that our viral approach are specific to the cerebellum, ruling out off-target demyelination elsewhere in the CNS as a contributor to the behavioral and synchrony phenotypes. We have added these descriptions in Result (lines 262-264)

(2) Characterize the gross morphology of the cerebellum at different developmental stages. Are major cell types all present? Major pathways preserved? 

We thank the reviewer for requesting additional evidence. To ensure that the developmental loss of oligodendrocytes did not globally disturb cerebellar architecture, we performed a comprehensive histological and electrophysiological survey during development. New data are presented (new Fig. S1–S2, Fig. 3E-H).

(1) Overall morphology. Low-magnification parvalbumin counterstaining revealed similar cerebellar area in DTA versus control mice at every age (Fig. S1F, G).

(2) Major neuronal classes. Quantification of parvalbumin-positive Purkinje cells and interneurons showed no differences in density between control and DTA (Fig. S2E, H, M, N, P). Purkinje dendritic arbors were not different between control and DTA (Fig. S2G, O).

(3) Excitatory and inhibitory synapse inputs. Miniature IPSCs and Parallel-fiber-EPSCs onto Purkinje cells were quantified; neither was differed between groups (Fig. 3E-G).

(4) Glial populations. IBA1-positive microglia and S100β-positive astrocytes exhibited normal density and marker intensity (Fig. S2).

Taken together, these analyses show that all major cell types are present at normal density, synaptic inputs from excitatory and inhibitory neurons are preserved, and gross cerebellar morphology is intact after DTA-mediated oligodendrocyte ablation.

(3) Recording of PNs to see whether the lack of synchrony is due to CFs or simple spikes.

We thank the reviewer for drawing attention to the work of Ramirez & Stell (2016), which showed that simple-spike bursts can elicit Ca²⁺ rises, but only in the soma and proximal dendrites of adult Purkinje cells. In our study, Regions of Interest were restricted to the dendritic arbor, where SS-evoked signals are essentially undetectable (Ramirez & Stell, 2016), whereas climbing-fiber complex spikes generate large, all-or-none transients (Good et al., 2017). Accordingly, even if a rare SS-driven event reached threshold it would likely fall outside our ROIs.

In addition, we directly imaged CF population activity by expressing GCaMP7f in inferior-olive neurons. Correlation analysis of CF boutons revealed that DTA ablation lowers CF–CF synchrony at P14 (new Fig. 3A–D). Because CF synchrony is a principal driver of Purkinje-cell co-activation, this reduction provides a mechanistic link between oligodendrocyte loss and the hyposynchrony we observe among Purkinje cells. Consistent with this interpretation, electrophysiological recordings showed that parallel-fiber EPSCs and inhibitory synaptic inputs onto Purkinje cells were unchanged by DTA treatment (Fig. 3E-H) , which makes it less likely that the reduced synchrony simply reflects changes in other excitatory or inhibitory synaptic drive.

That said, SS-dependent somatic Ca²⁺ signals could still influence downstream plasticity and long-term cerebellar function. In future work we therefore plan to combine somatic imaging with stage-specific oligodendrocyte manipulations to test whether SS-evoked Ca²⁺ dynamics are themselves modulated by oligodendrocyte support. We have added these descriptions in the Results (lines 301–312) and Discussion (lines 423–434).

(4) Is CF synapse elimination altered? Test using evoked EPSCs or staining methods.

We agree that directly testing whether oligodendrocyte loss disturbs climbing-fiber synapse elimination would provide a full mechanistic picture. We are already quantifying climbing fiber terminal number with vGluT2 immunostaining and recording evoked CF-EPSCs in the same DTA model; these data, together with an analysis of how population synchrony is involved in synapse elimination, will form the basis of a separate manuscript now in preparation. To keep the present paper focused on the phenomena we have rigorously documented—transient oligodendrocyte loss and the resulting long-lasting hyposynchrony and abnormal behaviors—we have removed the speculative sentence on oligodendrocyte-mediated synapse elimination. We believe this revision meets the reviewer’s request without over-extending the current dataset.

Thank you once again for your constructive suggestions and comments. We believe these changes have improved the clarity and readability of our manuscript.

Author response:

Reviewer #1

(1) The main weakness is that the study is wholly in vitro, using cultured hippocampal neurons.

We appreciate this reviewer's concern about the limitation of cultured hippocampal neurons in extracting disease-related spine phenotypes. While we fully recognize this limitation, we consider that this in vitro system has several advantages that contribute to translational research on mental disorders.

First, our culture system has been shown to support the development of spine morphology similar to that of the hippocampal CA1 excitatory synapse in vivo. High-resolution imaging techniques confirmed that the in vitro spine structure was highly preserved compared with in vivo preparations (Kashiwagi et al., Nature Communications, 2019). The present study used the same culture system and SIM imaging. Therefore, the difference we detected in samples derived from disease models is likely to reflect impairment of molecular mechanisms underlying native structural development in vivo.

Second, super-resolution imaging of thousands of spines in tissue preparations under precisely controlled conditions cannot be practically applied using currently available techniques. The advantage of our imaging and analytical pipeline is its reproducibility, which enabled us to compare the spine population data from eight different mouse models without normalization.

Third, a reduced culture system can demonstrate the direct effects of gene mutations on synapse phenotypes, independent of environmental influences. This property is highly advantageous for screening chemical compounds that rescue spine phenotypes. Neuronal firing patterns and receptor functions can also be easily controlled in a culture system. The difference in spine structure between ASD and schizophrenia mouse models is valuable information to establish a drug screening system.

Fourth, establishing an in vitro system for evaluating synapse phenotypes could reduce the need for animal experiments. Researchers should be aware of the 3Rs principles. In the future, combined with differentiation techniques for human iPS cells, our in vitro approach will enable the evaluation of disease-related spine phenotypes without the need for animal experiments. The effort to establish a reliable culture system should not be eliminated.

(2) Another weakness is that CaMKIIαK42R/K42R mutant mice are presented as a schizophrenia model.

We agree with this reviewer that CAMK2A mutations in humans are linked to multiple mental disorders, including developmental disorders, ASD, and schizophrenia. Association of gene mutations with the categories of mental disorders is not straightforward, as the symptoms of these disorders also overlap with each other. For the CaMKIIα K42R/K42R mutant, we considered the following points in its characterization as a model of mental disorder. Analysis of CaMKIIα +/- mice in Dr. Tsuyoshi Miyakawa's lab has provided evidence for the reduced CaMKIIα in schizophrenia-related phenotypes (Yamasaki et al., Mol Brain 2008; Frankland et al., Mol Brain Editorial 2008). It is also known that the CaMKIIα R8H mutation in the kinase domain is linked to schizophrenia (Brown et al., 2021). Both CaMKIIα R8H and CaMKIIα K42R mutations are located in the N-terminal domain and eliminate kinase activity. On the other hand, the representative CaMKIIα E183V mutation identified in ASD patients exhibits unique characteristics, including reduced kinase activity, decreased protein stability and expression levels, and disrupted interactions with ASD-associated proteins such as Shank3 (Stephenson et al., 2017). Importantly, reduced dendritic spines in neurons expressing CaMKIIα E183V is a property opposite to that of the CaMKIIα K42R/K42R mutant, which showed increased spine density (Koeberle et al. 2017).

Different CAMK2A mutations likely cause distinct phenotypes observed in the broad spectrum of mental disorders. In the revised manuscript, we will include a discussion of the relevant literature to categorize this mouse model appropriately.

References related to this discussion.

(1) Yamasaki et al., Mol Brain. 2008 DOI: 10.1186/1756-6606-1-6

(2) Frankland et al. Mol Brain. 2008 DOI: 10.1186/1756-6606-1-5

(3) Stephenson et al., J Neurosci. 2017 DOI: 10.1523/JNEUROSCI.2068-16.2017

(4) Koeberle et al. Sci Rep. 2017 DOI: 10.1038/s41598-017-13728-y

(5) Brown et al., iScience. 2021 DOI: 10.1016/j.isci.2021.103184

Reviewer #2

We recognize the reviewer's comments as important for improving our manuscript. We outline our general approach to addressing major concerns. Detailed responses to each point, along with additional data, will be provided in a formal revised manuscript.

(1) Demonstrating the robustness of statistical analyses

We appreciate this reviewer's concern about our strategies for the quantitative analysis of the large spine population. For the PCA analysis (Point 2), our preliminary results indicated that including all parameters or the selected five parameters did not make a significant difference in the relative placement of spines with specific morphologies in the feature space defined by the principal components. This point will be discussed in the revised manuscript. The potential problem of selecting a particular region within a feature space for spine shape analysis (Point 1) can be addressed by using alternative simulation-based approaches, such as bootstrap or permutation tests. These analyses will be included in the revised manuscript. The use of sample numbers in statistical analyses should align with the analysis's purpose (Point 3). When analyzing the distribution of samples in the feature space, it is necessary to use spine numbers for statistical assessment. We will recheck the statistical methods and apply the appropriate method for each analysis. The spine population data in Figures 2 and 8 cannot be directly compared, as the spine visualization methods differ (Figure 2 with membrane DiI labeling; Figure 8 with cytoplasmic GFP labeling) (Point 9). Spine populations of the same size are inevitably plotted in different feature spaces. This point will be discussed more clearly in the revised manuscript.

(2) Clarification of experimental conditions and data reliability

Per this reviewer's suggestion, we will provide more information on the genetic background of mice and the differences in spine structure from DIV 18-22 (Points 4 and 5). We will also provide additional validation data for the functional analyses using knockdown and overexpression methods, for which we already have preliminary data (Point 7). Concerns about the interpretation of data obtained from in vitro culture (Point 12), raised by this reviewer, are also noted by reviewer #1. As explained in the response to reviewer #1, we intentionally selected an in vitro culture system to analyze multiple samples derived from mouse models of mental disorders for several reasons. Nevertheless, we will revise the discussion and incorporate the points this reviewer raised regarding the disadvantages of in vitro systems.

(3) Validation of biological mechanisms and interpretation

In the computational modeling (Point 6), we started from the data of spine turnover (excluding the data of spine volume increase/decrease), fitted the model with the data, and found that the best-fit model showed three features: fast spine turnover, lower spine density, and smaller size of transient spines in schizophrenia mouse models. As the reviewer noted, information about spine turnover is already present in the input data. However, the other two properties are generated independently of the input data, indicating the value of this model. We plan to add additional confirmatory analyses to this model in the revised manuscript.

In response to Point 8, we will provide supporting data on the functional role of Ecgr4 in synapse regulation. We will also refine our discussion on the ASD and Schizophrenia phenotypes based on the suggested literature (Points 10 and 11). Quantification of the initial growth of spines is technically demanding, as it requires higher imaging frequency and longer time-lapse recordings to capture rare events. It is difficult to conclude which of the two possibilities, slow spine growth or initial size differences, is correct, based on our available data. This point will be discussed in the revised manuscript (Point 13).

Author response:

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

eLife Assessment

This study examines a valuable question regarding the developmental trajectory of neural mechanisms supporting facial expression processing. Leveraging a rare intracranial EEG (iEEG) dataset including both children and adults, the authors reported that facial expression recognition mainly engaged the posterior superior temporal cortex (pSTC) among children, while both pSTC and the prefrontal cortex were engaged among adults. However, the sample size is relatively small, with analyses appearing incomplete to fully support the primary claims. 

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates how the brain processes facial expressions across development by analyzing intracranial EEG (iEEG) data from children (ages 5-10) and post-childhood individuals (ages 13-55). The researchers used a short film containing emotional facial expressions and applied AI-based models to decode brain responses to facial emotions. They found that in children, facial emotion information is represented primarily in the posterior superior temporal cortex (pSTC) - a sensory processing area - but not in the dorsolateral prefrontal cortex (DLPFC), which is involved in higher-level social cognition. In contrast, post-childhood individuals showed emotion encoding in both regions. Importantly, the complexity of emotions encoded in the pSTC increased with age, particularly for socially nuanced emotions like embarrassment, guilt, and pride. The authors claim that these findings suggest that emotion recognition matures through increasing involvement of the prefrontal cortex, supporting a developmental trajectory where top-down modulation enhances understanding of complex emotions as children grow older.

Strengths:

(1) The inclusion of pediatric iEEG makes this study uniquely positioned to offer high-resolution temporal and spatial insights into neural development compared to non-invasive approaches, e.g., fMRI, scalp EEG, etc.

(2) Using a naturalistic film paradigm enhances ecological validity compared to static image tasks often used in emotion studies.

(3) The idea of using state-of-the-art AI models to extract facial emotion features allows for high-dimensional and dynamic emotion labeling in real time

Weaknesses:

(1) The study has notable limitations that constrain the generalizability and depth of its conclusions. The sample size was very small, with only nine children included and just two having sufficient electrode coverage in the posterior superior temporal cortex (pSTC), which weakens the reliability and statistical power of the findings, especially for analyses involving age

We appreciated the reviewer’s point regarding the constrained sample size.

As an invasive method, iEEG recordings can only be obtained from patients undergoing electrode implantation for clinical purposes. Thus, iEEG data from young children are extremely rare,  and rapidly increasing the sample size within a few years is not feasible. However, we are confident in the reliability of our main conclusions. Specifically, 8 children (53 recording contacts in total) and 13 control participants (99 recording contacts in total) with electrode coverage in the DLPFC are included in our DLPFC analysis. This sample size is comparable to other iEEG studies with similar experiment designs [1-3]. 

For pSTC, we returned to the data set and found another two children who had pSTC coverage. After involving these children’s data, the group-level analysis using permutation test showed that children’s pSTC significantly encode facial emotion in naturalistic contexts (Figure 3B). Notably, the two new children’s (S33 and S49) responses were highly consistent with our previous observations. Moreover, the averaged prediction accuracy in children’s pSTC (r_speech=0.1565) was highly comparable to that in post-childhood group (r_speech=0.1515).

(1) Zheng, J. et al. Multiplexing of Theta and Alpha Rhythms in the Amygdala-Hippocampal Circuit Supports Pafern Separation of Emotional Information. Neuron 102, 887-898.e5 (2019).

(2) Diamond, J. M. et al. Focal seizures induce spatiotemporally organized spiking activity in the human cortex. Nat. Commun. 15, 7075 (2024).

(3) Schrouff, J. et al. Fast temporal dynamics and causal relevance of face processing in the human temporal cortex. Nat. Commun. 11, 656 (2020).

(2) Electrode coverage was also uneven across brain regions, with not all participants having electrodes in both the dorsolateral prefrontal cortex (DLPFC) and pSTC, and most coverage limited to the left hemisphere-hindering within-subject comparisons and limiting insights into lateralization.

The electrode coverage in each patient is determined entirely by the clinical needs. Only a few patients have electrodes in both DLPFC and pSTC because these two regions are far apart, so it’s rare for a single patient’s suspected seizure network to span such a large territory. However, it does not affect our results, as most iEEG studies combine data from multiple patients to achieve sufficient electrode coverage in each target brain area. As our data are mainly from left hemisphere (due to the clinical needs), this study was not designed to examine whether there is a difference between hemispheres in emotion encoding. Nevertheless, lateralization remains an interesting question that should be addressed in future research, and we have noted this limitation in the Discussion (Page 8, in the last paragraph of the Discussion).

(3) The developmental differences observed were based on cross-sectional comparisons rather than longitudinal data, reducing the ability to draw causal conclusions about developmental trajectories.  

In the context of pediatric intracranial EEG, longitudinal data collection is not feasible due to the invasive nature of electrode implantation. We have added this point to the Discussion to acknowledge that while our results reveal robust age-related differences in the cortical encoding of facial emotions, longitudinal studies using non-invasive methods will be essential to directly track developmental trajectories (Page 8, in the last paragraph of Discussion). In addition, we revised our manuscript to avoid emphasis causal conclusions about developmental trajectories in the current study (For example, we use “imply” instead of “suggest” in the fifth paragraph of Discussion).

(4) Moreover, the analysis focused narrowly on DLPFC, neglecting other relevant prefrontal areas such as the orbitofrontal cortex (OFC) and anterior cingulate cortex (ACC), which play key roles in emotion and social processing.

We agree that both OFC and ACC are critically involved in emotion and social processing. However, we have no recordings from these areas because ECoG rarely covers the ACC or OFC due to technical constraints. We have noted this limitation in the Discussion(Page 8, in the last paragraph of Discussion). Future follow-up studies using sEEG or non-invasive imaging methods could be used to examine developmental patterns in these regions.

(5) Although the use of a naturalistic film stimulus enhances ecological validity, it comes at the cost of experimental control, with no behavioral confirmation of the emotions perceived by participants and uncertain model validity for complex emotional expressions in children. A nonfacial music block that could have served as a control was available but not analyzed. 

The facial emotion features used in our encoding models were extracted by Hume AI models, which were trained on human intensity ratings of large-scale, experimentally controlled emotional expression data[1-2]. Thus, the outputs of Hume AI model reflect what typical facial expressions convey, that is, the presented facial emotion. Our goal of the present study was to examine how facial emotions presented in the videos are encoded in the human brain at different developmental stages. We agree that children’s interpretation of complex emotions may differ from that of adults, resulting in different perceived emotion (i.e., the emotion that the observer subjectively interprets). Behavioral ratings are necessary to study the encoding of subjectively perceived emotion, which is a very interesting direction but beyond the scope of the present work. We have added a paragraph in the Discussion (see Page 8) to explicitly note that our study focused on the encoding of presented emotion.

We appreciated the reviewer’s point regarding the value of non-facial music blocks. However,  although there are segments in music condition that have no faces presented, these cannot be used as a control condition to test whether the encoding model’s prediction accuracy in pSTC or DLPFC drops to chance when no facial emotion is present. This is because, in the absence of faces, no extracted emotion features are available to be used for the construction of encoding model (see Author response image 1 below).  Thus, we chose to use a different control analysis for the present work. For children’s pSTC, we shuffled facial emotion feature in time to generate a null distribution, which was then used to test the statistical significance of the encoding models (see Methods/Encoding model fitting for details).

(1) Brooks, J. A. et al. Deep learning reveals what facial expressions mean to people in different cultures. iScience 27, 109175 (2024).

(2) Brooks, J. A. et al. Deep learning reveals what vocal bursts express in different cultures. Nat. Hum. Behav. 7, 240–250 (2023).

Author response image 1.

Time courses of Hume AI extracted facial expression features for the first block of music condition. Only top 5 facial expressions were shown here to due to space limitation.

(6) Generalizability is further limited by the fact that all participants were neurosurgical patients, potentially with neurological conditions such as epilepsy that may influence brain responses. 

We appreciated the reviewer’s point. However, iEEG data can only be obtained from clinical populations (usually epilepsy patients) who have electrodes implantation.  Given current knowledge about focal epilepsy and its potential effects on brain activity, researchers believe that epilepsy-affected brains can serve as a reasonable proxy for normal human brains when confounding influences are minimized through rigorous procedures[1]. In our study, we took several steps to ensure data quality: (1) all data segments containing epileptiform discharges were identified and removed at the very beginning of preprocessing, (2) patients were asked to participate the experiment several hours outside the window of seizures. Please see Method for data quality check description (Page 9/ Experimental procedures and iEEG data processing). 

(1) Parvizi J, Kastner S. 2018. Promises and limitations of human intracranial electroencephalography. Nat Neurosci 21:474–483. doi:10.1038/s41593-018-0108-2

(7) Additionally, the high temporal resolution of intracranial EEG was not fully utilized, as data were down-sampled and averaged in 500-ms windows.  

We agree that one of the major advantages of iEEG is its millisecond-level temporal resolution. In our case, the main reason for down-sampling was that the time series of facial emotion features extracted from the videos had a temporal resolution of 2 Hz, which were used for the modelling neural responses. In naturalistic contexts, facial emotion features do not change on a millisecond timescale, so a 500 ms window is sufficient to capture the relevant dynamics. Another advantage of iEEG is its tolerance to motion, which is excessive in young children (e.g., 5-year-olds). This makes our dataset uniquely valuable, suggesting robust representation in the pSTC but not in the DLPFC in young children. Moreover, since our method framework (Figure 1) does not rely on high temporal resolution method, so it can be transferred to non-invasive modalities such as fMRI, enabling future studies to test these developmental patterns in larger populations.

(8) Finally, the absence of behavioral measures or eye-tracking data makes it difficult to directly link neural activity to emotional understanding or determine which facial features participants afended to.  

We appreciated this point. Part of our rationale is presented in our response to (5) for the absence of behavioral measures. Following the same rationale, identifying which facial features participants attended to is not necessary for testing our main hypotheses because our analyses examined responses to the overall emotional content of the faces. However, we agree and recommend future studies use eye-tracking and corresponding behavioral measures in studies of subjective emotional understanding. 

Reviewer #2 (Public review):

Summary:

In this paper, Fan et al. aim to characterize how neural representations of facial emotions evolve from childhood to adulthood. Using intracranial EEG recordings from participants aged 5 to 55, the authors assess the encoding of emotional content in high-level cortical regions. They report that while both the posterior superior temporal cortex (pSTC) and dorsolateral prefrontal cortex (DLPFC) are involved in representing facial emotions in older individuals, only the pSTC shows significant encoding in children. Moreover, the encoding of complex emotions in the pSTC appears to strengthen with age. These findings lead the authors to suggest that young children rely more on low-level sensory areas and propose a developmental shiZ from reliance on lower-level sensory areas in early childhood to increased top-down modulation by the prefrontal cortex as individuals mature.

Strengths: 

(1) Rare and valuable dataset: The use of intracranial EEG recordings in a developmental sample is highly unusual and provides a unique opportunity to investigate neural dynamics with both high spatial and temporal resolution. 

(2) Developmentally relevant design: The broad age range and cross-sectional design are well-suited to explore age-related changes in neural representations. 

(3) Ecological validity: The use of naturalistic stimuli (movie clips) increases the ecological relevance of the findings. 

(4) Feature-based analysis: The authors employ AIbased tools to extract emotion-related features from naturalistic stimuli, which enables a data-driven approach to decoding neural representations of emotional content. This method allows for a more fine-grained analysis of emotion processing beyond traditional categorical labels. 

Weaknesses: 

(1) The emotional stimuli included facial expressions embedded in speech or music, making it difficult to isolate neural responses to facial emotion per se from those related to speech content or music-induced emotion. 

We thank the reviewer for their raising this important point. We agree that in naturalistic settings, face often co-occur with speech, and that these sources of emotion can overlap. However, background music induced emotions have distinct temporal dynamics which are separable from facial emotion (See the Author response image 2 (A) and (B) below). In addition, face can convey a wide range of emotions (48 categories in Hume AI model), whereas music conveys far fewer (13 categories reported by a recent study [1]). Thus, when using facial emotion feature time series as regressors (with 48 emotion categories and rapid temporal dynamics), the model performance will reflect neural encoding of facial emotion in the music condition, rather than the slower and lower-dimensional emotion from music. 

For the speech condition, we acknowledge that it is difficult to fully isolate neural responses to facial emotion from those to speech when the emotional content from faces and speech highly overlaps. However, in our study, (1) the time courses of emotion features from face and voice are still different (Author response image 2 (C) and (D)), (2) our main finding that DLPFC encodes facial expression information in postchildhood individuals but not in young children was found in both speech and music condition (Figure 2B and 2C). In music condition, neural responses to facial emotion are not affected by speech. Thus, we have included the DLPFC results from the music condition in the revised manuscript (Figure 2C), and we acknowledge that this issue should be carefully considered in future studies using videos with speech, as we have indicated in the future directions in the last paragraph of Discussion.

(1) Cowen, A. S., Fang, X., Sauter, D. & Keltner, D. What music makes us feel: At least 13 dimensions organize subjective experiences associated with music across different cultures. Proc Natl Acad Sci USA 117, 1924–1934 (2020).

Author response image 2.

Time courses of the amusement. (A) and (B) Amusement conveyed by face or music in a 30-s music block. Facial emotion features are extracted by Hume AI. For emotion from music, we approximated the amusement time course using a weighted combination of low-level acoustic features (RMS energy, spectral centroid, MFCCs), which capture intensity, brightness, and timbre cues linked to amusement. Notice that music continues when there are no faces presented. (C) and (D) Amusement conveyed by face or voice in a 30-s speech block. From 0 to 5 seconds, a girl is introducing her friend to a stranger. The camera focuses on the friend, who appears nervous, while the girl’s voice sounds cheerful. This mismatch explains why the shapes of the two time series differ at the beginning. Such situations occur frequently in naturalistic movies

(2) While the authors leveraged Hume AI to extract facial expression features from the video stimuli, they did not provide any validation of the tool's accuracy or reliability in the context of their dataset. It remains unclear how well the AI-derived emotion ratings align with human perception, particularly given the complexity and variability of naturalistic stimuli. Without such validation, it is difficult to assess the interpretability and robustness of the decoding results based on these features.  

Hume AI models were trained and validated by human intensity ratings of large-scale, experimentally controlled emotional expression data [1-2]. The training process used both manual annotations from human raters and deep neural networks. Over 3000 human raters categorized facial expressions into emotion categories and rated on a 1-100 intensity scale. Thus, the outputs of Hume AI model reflect what typical facial expressions convey (based on how people actually interpret them), that is, the presented facial emotion. Our goal of the present study was to examine how facial emotions presented in the videos are encoded in the human brain at different developmental stages. We agree that the interpretation of facial emotions may be different in individual participants, resulting in different perceived emotion (i.e., the emotion that the observer subjectively interprets). Behavioral ratings are necessary to study the encoding of subjectively perceived emotion, which is a very interesting direction but beyond the scope of the present work. We have added text in the Discussion to explicitly note that our study focused on the encoding of presented emotion (second paragraph in Page 8).

(1) Brooks, J. A. et al. Deep learning reveals what facial expressions mean to people in different cultures. iScience 27, 109175 (2024).

(2) Brooks, J. A. et al. Deep learning reveals what vocal bursts express in different cultures. Nat. Hum. Behav. 7, 240–250 (2023).

(3) Only two children had relevant pSTC coverage, severely limiting the reliability and generalizability of results.  

We appreciated this point and agreed with both reviewers who raised it as a significant concern. As described in response to reviewer 1 (comment 1), we have added data from another two children who have pSTC coverage. Group-level analysis using permutation test showed that children’s pSTC significantly encode facial emotion in naturalistic contexts (Figure 3B). Because iEEG data from young children are extremely rare, rapidly increasing the sample size within a few years is not feasible. However, we are confident in the reliability of our conclusion that children’s pSTC can encode facial emotion. First,  the two new children’s responses (S33 and S49) from pSTC were highly consistent with our previous observations (see individual data in Figure 3B). Second, the averaged prediction accuracy in children’s pSTC (r_speech=0.1565) was highly comparable to that in post-childhood group (r_speech=0.1515).

(4) The rationale for focusing exclusively on high-frequency activity for decoding emotion representations is not provided, nor are results from other frequency bands explored.   

We focused on high-frequency broadband (HFB) activity because it is widely considered to reflect the responses of local neuronal populations near the recording electrode, whereas low-frequency oscillations in the theta, alpha, and beta ranges are thought to serve as carrier frequencies for long-range communication across distributed networks[1-2]. Since our study aimed to examine the representation of facial emotion in localized cortical regions (DLPFC and pSTC), HFB activity provides the most direct measure of the relevant neural responses. We have added this rationale to the manuscript (Page 3).

(1) Parvizi, J. & Kastner, S. Promises and limitations of human intracranial electroencephalography. Nat. Neurosci. 21, 474–483 (2018).

(2) Buzsaki, G. Rhythms of the Brain. (Oxford University Press, Oxford, 200ti).

(5) The hypothesis of developmental emergence of top-down prefrontal modulation is not directly tested. No connectivity or co-activation analyses are reported, and the number of participants with simultaneous coverage of pSTC and DLPFC is not specified.  

Directional connectivity analysis results were not shown because only one child has simultaneous coverage of pSTC and DLPFC. However, the  Granger Causality results from post-childhood group (N=7) clearly showed that the influence in the alpha/beta band from DLPFC to pSTC (top-down) is gradually increased above the onset of face presentation (Author response image 3, below left, plotted in red). By comparison, the influence in the alpha/beta band from pSTC to DLPFC (bottom-up) is gradually decreased after the onset of face presentation (Author response image 3, below left, blue curve). The influence in alpha/beta band from DLPFC to pSTC was significantly increased at 750 and 1250 ms after the face presentation (face vs nonface, paired t-test, Bonferroni  corrected P=0.005, 0.006), suggesting an enhanced top-down modulation in the post-childhood group during watching emotional faces. Interestingly, this top-down influence appears very different in the 8-year-old child at 1250 ms after the face presentation (Author response image 3, below left, black curve).

As we cannot draw direct conclusions from the single-subject sample presented here, the top-down hypothesis is introduced only as a possible explanation for our current results. We have removed potentially misleading statements, and we plan to test this hypothesis directly using MEG in the future.

Author response image 3.

Difference of Granger causality indices (face – nonface) in alpha/beta and gamma band for both directions. We identified a series of face onset in the movie that paticipant watched. Each trial was defined as -0.1 to 1.5 s relative to the onset. For the non-face control trials, we used houses, animals and scenes. Granger causality was calculated for 0-0.5 s, 0.5-1 s and 1-1.5 s time window. For the post-childhood group, GC indices were averaged across participants. Error bar is sem.

(6) The "post-childhood" group spans ages 13-55, conflating adolescence, young adulthood, and middle age. Developmental conclusions would benefit from finer age stratification.  

We appreciate this insightful comment. Our current sample size does not allow such stratification. But we plan to address this important issue in future MEG studies with larger cohorts.

(7) The so-called "complex emotions" (e.g., embarrassment, pride, guilt, interest) used in the study often require contextual information, such as speech or narrative cues, for accurate interpretation, and are not typically discernible from facial expressions alone. As such, the observed age-related increase in neural encoding of these emotions may reflect not solely the maturation of facial emotion perception, but rather the development of integrative processing that combines facial, linguistic, and contextual cues. This raises the possibility that the reported effects are driven in part by language comprehension or broader social-cognitive integration, rather than by changes in facial expression processing per se.  

We agree with this interpretation. Indeed, our results already show that speech influences the encoding of facial emotion in the DLPFC differently in the childhood and post-childhood groups (Figure 2D), suggesting that children’s ability to integrate multiple cues is still developing. Future studies are needed to systematically examine how linguistic cues and prior experiences contribute to the understanding of complex emotions from faces, which we have added to our future directions section (last paragraph in Discussion, Page 8-9 ).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

In the introduction: "These neuroimaging data imply that social and emotional experiences shape the prefrontal cortex's involvement in processing the emotional meaning of faces throughout development, probably through top-down modulation of early sensory areas." Aren't these supposed to be iEEG data instead of neuroimaging? 

Corrected.

Reviewer #2 (Recommendations for the authors):

This manuscript would benefit from several improvements to strengthen the validity and interpretability of the findings:

(1) Increase the sample size, especially for children with pSTC coverage. 

We added data from another two children who have pSTC coverage. Please see our response to reviewer 2’s comment 3 and reviewer 1’s comment 1.

(2) Include directional connectivity analyses to test the proposed top-down modulation from DLPFC to pSTC. 

Thanks for the suggestion. Please see our response to reviewer 2’s comment 5.

(3) Use controlled stimuli in an additional experiment to separate the effects of facial expression, speech, and music. 

This is an excellent point. However, iEEG data collection from children is an exceptionally rare opportunity and typically requires many years, so we are unable to add a controlled-stimulus experiment to the current study. We plan to consider using controlled stimuli to study the processing of complex emotion using non-invasive method in the future. In addition, please see our response to reviewer 2’s comment 1 for a description of how neural responses to facial expression and music are separated in our study.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary

This is a strong paper that presents a clear advance in multi-animal tracking. The authors introduce an updated version of idtracker.ai that reframes identity assignment as a contrastive learning problem rather than a classification task requiring global fragments. This change leads to gains in speed and accuracy. The method eliminates a known bottleneck in the original system, and the benchmarking across species is comprehensive and well executed. I think the results are convincing and the work is significant.

Strengths

The main strengths are the conceptual shift from classification to representation learning, the clear performance gains, and the fact that the new version is more robust. Removing the need for global fragments makes the software more flexible in practice, and the accuracy and speed improvements are well demonstrated. The software appears thoughtfully implemented, with GUI updates and integration with pose estimators.

Weaknesses

I don't have any major criticisms, but I have identified a few points that should be addressed to improve the clarity and accuracy of the claims made in the paper.

(1) The title begins with "New idtracker.ai," which may not age well and sounds more promotional than scientific. The strength of the work is the conceptual shift to contrastive representation learning, and it might be more helpful to emphasize that in the title rather than branding it as "new."

We considered using “Contrastive idtracker.ai”. However, we thought that readers could then think that we believe they could use both the old idtracker.ai or this contrastive version. But we want to say that the new version is the one to use as it is better in both accuracy and tracking times. We think “New idtracker.ai” communicates better that this version is the version we recommend.

(2) Several technical points regarding the comparison between TRex (a system evaluated in the paper) and idtracker.ai should be addressed to ensure the evaluation is fair and readers are fully informed.

(2.1) Lines 158-160: The description of TRex as based on "Protocol 2 of idtracker.ai" overlooks several key additions in TRex, such as posture image normalization, tracklet subsampling, and the use of uniqueness feedback during training. These features are not acknowledged, and it's unclear whether TRex was properly configured - particularly regarding posture estimation, which appears to have been omitted but isn't discussed. Without knowing the actual parameters used to make comparisons, it's difficult to dassess how the method was evaluated.

We added the information about the key additions of TRex in the section “The new idtracker.ai uses representation learning”, lines 153-157. Posture estimation in TRex was not explicitly used but neither disabled during the benchmark; we clarified this in the last paragraph of “Benchmark of accuracy and tracking time”, lines 492-495.

(2.2) Lines 162-163: The paper implies that TRex gains speed by avoiding Protocol 3, but in practice, idtracker.ai also typically avoids using Protocol 3 due to its extremely long runtime. This part of the framing feels more like a rhetorical contrast than an informative one.

We removed this, see new lines 153-157.

(2.3) Lines 277-280: The contrastive loss function is written using the label l, but since it refers to a pair of images, it would be clearer and more precise to write it as l_{I,J}. This would help readers unfamiliar with contrastive learning understand the formulation more easily.

We added this change in lines 613-620.

(2.4) Lines 333-334: The manuscript states that TRex can fail to track certain videos, but this may be inaccurate depending on how the authors classify failures. TRex may return low uniqueness scores if training does not converge well, but this isn't equivalent to tracking failure. Moreover, the metric reported by TRex is uniqueness, not accuracy. Equating the two could mislead readers. If the authors did compare outputs to human-validated data, that should be stated more explicitly.

We observed TRex crashing without outputting any trajectories on some occasions (Appendix 1—figure 1), and this is what we labeled as “failure”. These failures happened in the most difficult videos of our benchmark, that’s why we treated them the same way as idtracker.ai going to P3. We clarified this in new lines 464-469.

The accuracy measured in our benchmark is not estimated but it is human-validated (see section Computation of tracking accuracy in Appendix 1). Both softwares report some quality estimators at the end of a tracking (“estimated accuracy” for idtracker.ai and "uniqueness” for TRex) but these were not used in the benchmark.

(2.5) Lines 339-341: The evaluation approach defines a "successful run" and then sums the runtime across all attempts up to that point. If success is defined as simply producing any output, this may not reflect how experienced users actually interact with the software, where parameters are iteratively refined to improve quality.

Yes, our benchmark was designed to be agnostic to the different experiences of the user. Also, our benchmark was designed for users that do not inspect the trajectories to choose parameters again not to leave room for potential subjectivity.

(2.6) Lines 344-346: The simulation process involves sampling tracking parameters 10,000 times and selecting the first "successful" run. If parameter tuning is randomized rather than informed by expert knowledge, this could skew the results in favor of tools that require fewer or simpler adjustments. TRex relies on more tunable behavior, such as longer fragments improving training time, which this approach may not capture.

We precisely used the TRex parameter track_max_speed to elongate fragments for optimal tracking. Rather than randomized parameter tuning, we defined the “valid range” for this parameter so that all values in it would produce a decent fragment structure. We used this procedure to avoid worsening those methods that use more parameters.

(2.7) Line 354 onward: TRex was evaluated using two varying parameters (threshold and track_max_speed), while idtracker.ai used only one (intensity_threshold). With a fixed number of samples, this asymmetry could bias results against TRex. In addition, users typically set these parameters based on domain knowledge rather than random exploration.

idtracker.ai and TRex have several parameters. Some of them have a single correct value (e.g. number of animals) or the default value that the system computes is already good (e.g. minimum blob size). For a second type of parameters, the system finds a value that is in general not as good, so users need to modify them. In general, users find that for this second type of parameter there is a valid interval of possible values, from which they need to choose a single value to run the system. idtracker.ai has intensity_threshold as the only parameter of this second type and TRex has two: threshold and track_max_speed. For these parameters, choosing one value or another within the valid interval can give different tracking results. Therefore, when we model a user that wants to run the system once except if it goes to P3 (idtracker.ai) or except if it crashes (TRex), it is these parameters we sample from within the valid interval to get a different value for each run of the system. We clarify this in lines 452-469 of the section “Benchmark of accuracy and tracking time”.

Note that if we chose to simply run old idtracker.ai (v4 or v5) or TRex a single time, this would benefit the new idtracker.ai (v6). This is because old idtracker.ai can enter the very slow protocol 3 and TRex can fail to track. So running old idtracker.ai or TRex up to 5 times until old idtracker.ai does not use Protocol 3 and TRex does not fail is to make them as good as they can be with respect to the new idtracker.ai. 

(2.8) Figure 2-figure supplement 3: The memory usage comparison lacks detail. It's unclear whether RAM or VRAM was measured, whether shared or compressed memory was included, or how memory was sampled. Since both tools dynamically adjust to system resources, the relevance of this comparison is questionable without more technical detail.

We modified the text in the caption (new Figure 1-figure supplement 2) adding the kind of memory we measured (RAM) and how we measured it. We already have a disclaimer for this plot saying that memory management depends on the machine's available resources. We agree that this is a simple analysis of the usage of computer resources.

(3) While the authors cite several key papers on contrastive learning, they do not use the introduction or discussion to effectively situate their approach within related fields where similar strategies have been widely adopted. For example, contrastive embedding methods form the backbone of modern facial recognition and other image similarity systems, where the goal is to map images into a latent space that separates identities or classes through clustering. This connection would help emphasize the conceptual strength of the approach and align the work with well-established applications. Similarly, there is a growing literature on animal re-identification (ReID), which often involves learning identity-preserving representations across time or appearance changes. Referencing these bodies of work would help readers connect the proposed method with adjacent areas using similar ideas, and show that the authors are aware of and building on this wider context.

We have now added a new section in Appendix 3, “Differences with previous work in contrastive/metric learning” (lines 792-841) to include references to previous work and a description of what we do differently.

(4) Some sections of the Results text (e.g., lines 48-74) read more like extended figure captions than part of the main narrative. They include detailed explanations of figure elements, sorting procedures, and video naming conventions that may be better placed in the actual figure captions or moved to supplementary notes. Streamlining this section in the main text would improve readability and help the central ideas stand out more clear

Thank you for pointing this out. We have rewritten the Results, for example streamlining the old lines 48-74 (new lines 42-48)  by moving the comments about names, files and order of videos to the caption of Figure 1.

Overall, though, this is a high-quality paper. The improvements to idtracker.ai are well justified and practically significant. Addressing the above comments will strengthen the work, particularly by clarifying the evaluation and comparisons.

We thank the reviewer for the detailed suggestions. We believe we have taken all of them into consideration to improve the ms.

Reviewer #2 (Public review):

Summary:

This work introduces a new version of the state-of-the-art idtracker.ai software for tracking multiple unmarked animals. The authors aimed to solve a critical limitation of their previous software, which relied on the existence of "global fragments" (video segments where all animals are simultaneously visible) to train an identification classifier network, in addition to addressing concerns with runtime speed. To do this, the authors have both re-implemented the backend of their software in PyTorch (in addition to numerous other performance optimizations) as well as moving from a supervised classification framework to a self-supervised, contrastive representation learning approach that no longer requires global fragments to function. By defining positive training pairs as different images from the same fragment and negative pairs as images from any two co-existing fragments, the system cleverly takes advantage of partial (but high-confidence) tracklets to learn a powerful representation of animal identity without direct human supervision. Their formulation of contrastive learning is carefully thought out and comprises a series of empirically validated design choices that are both creative and technically sound. This methodological advance is significant and directly leads to the software's major strengths, including exceptional performance improvements in speed and accuracy and a newfound robustness to occlusion (even in severe cases where no global fragments can be detected). Benchmark comparisons show the new software is, on average, 44 times faster (up to 440 times faster on difficult videos) while also achieving higher accuracy across a range of species and group sizes. This new version of idtracker.ai is shown to consistently outperform the closely related TRex software (Walter & Couzin, 2021\), which, together with the engineering innovations and usability enhancements (e.g., outputs convenient for downstream pose estimation), positions this tool as an advancement on the state-of-the-art for multi-animal tracking, especially for collective behavior studies.

Despite these advances, we note a number of weaknesses and limitations that are not well addressed in the present version of this paper:

Weaknesses

(1) The contrastive representation learning formulation. Contrastive representation learning using deep neural networks has long been used for problems in the multi-object tracking domain, popularized through ReID approaches like DML (Yi et al., 2014\) and DeepReID (Li et al., 2014). More recently, contrastive learning has become more popular as an approach for scalable self-supervised representation learning for open-ended vision tasks, as exemplified by approaches like SimCLR (Chen et al., 2020), SimSiam (Chen et al., 2020\), and MAE (He et al., 2021\) and instantiated in foundation models for image embedding like DINOv2 (Oquab et al., 2023). Given their prevalence, it is useful to contrast the formulation of contrastive learning described here relative to these widely adopted approaches (and why this reviewer feels it is appropriate):

(1.1) No rotations or other image augmentations are performed to generate positive examples. These are not necessary with this approach since the pairs are sampled from heuristically tracked fragments (which produces sufficient training data, though see weaknesses discussed below) and the crops are pre-aligned egocentrically (mitigating the need for rotational invariance).

(1.2) There is no projection head in the architecture, like in SimCLR. Since classification/clustering is the only task that the system is intended to solve, the more general "nuisance" image features that this architectural detail normally affords are not necessary here.

(1.3) There is no stop gradient operator like in BYOL (Grill et al., 2020\) or SimSiam. Since the heuristic tracking implicitly produces plenty of negative pairs from the fragments, there is no need to prevent representational collapse due to class asymmetry. Some care is still needed, but the authors address this well through a pair sampling strategy (discussed below).

(1.4) Euclidean distance is used as the distance metric in the loss rather than cosine similarity as in most contrastive learning works. While cosine similarity coupled with L2-normalized unit hypersphere embeddings has proven to be a successful recipe to deal with the curse of dimensionality (with the added benefit of bounded distance limits), the authors address this through a cleverly constructed loss function that essentially allows direct control over the intra- and inter-cluster distance (D\_pos and D\_neg). This is a clever formulation that aligns well with the use of K-means for the downstream assignment step.

No concerns here, just clarifications for readers who dig into the review. Referencing the above literature would enhance the presentation of the paper to align with the broader computer vision literature.

Thank you for this detailed comparison. We have now added a new section in Appendix 3, “Differences with previous work in contrastive/metric learning” (lines 792-841) to include references to previous work and a description of what we do differently, including the points raised by the reviewer.

(2) Network architecture for image feature extraction backbone. As most of the computations that drive up processing time happen in the network backbone, the authors explored a variety of architectures to assess speed, accuracy, and memory requirements. They land on ResNet18 due to its empirically determined performance. While the experiments that support this choice are solid, the rationale behind the architecture selection is somewhat weak. The authors state that: "We tested 23 networks from 8 different families of state-of-the-art convolutional neural network architectures, selected for their compatibility with consumer-grade GPUs and ability to handle small input images (20 × 20 to 100 × 100 pixels) typical in collective animal behavior videos."

(2.1) Most modern architectures have variants that are compatible with consumer-grade GPUs. This is true of, for example, HRNet (Wang et al., 2019), ViT (Dosovitskiy et al., 2020), SwinT (Liu et al., 2021), or ConvNeXt (Liu et al., 2022), all of which report single GPU training and fast runtime speeds through lightweight configuration or subsequent variants, e.g., MobileViT (Mehta et al., 2021). The authors may consider revising that statement or providing additional support for that claim (e.g., empirical experiments) given that these have been reported to outperform ResNet18 across tasks.

Following the recommendation of the reviewer, we tested the architectures SwinT, ConvNeXt and ViT. We found out that none of them outperformed ResNet18 since they all showed a slower learning curve. This would result in higher tracking times. These tests are now included in the section “Network architecture” (lines 550-611).

(2.2) The compatibility of different architectures with small image sizes is configurable. Most convolutional architectures can be readily adapted to work with smaller image sizes, including 20x20 crops. With their default configuration, they lose feature map resolution through repeated pooling and downsampling steps, but this can be readily mitigated by swapping out standard convolutions with dilated convolutions and/or by setting the stride of pooling layers to 1, preserving feature map resolution across blocks. While these are fairly straightforward modifications (and are even compatible with using pretrained weights), an even more trivial approach is to pad and/or resize the crops to the default image size, which is likely to improve accuracy at a possibly minimal memory and runtime cost. These techniques may even improve the performance with the architectures that the authors did test out.

The only two tested architectures that require a minimum image size are AlexNet and DenseNet. DenseNet proved to underperform ResNet18 in the videos where the images are sufficiently large. We have tested AlexNet with padded images to see that it also performs worse than ResNet18 (see Appendix 3—figure 1).

We also tested the initialization of ResNet18 with pre-trained weights from ImageNet (in Appendix 3—figure 2) and it proved to bring no benefit to the training speed (added in lines 591-592).

(2.3) The authors do not report whether the architecture experiments were done with pretrained or randomly initialized weights.

We adapted the text to make it clear that the networks are always randomly initialized (lines 591-592, lines 608-609 and the captions of Appendix 3—figure 1 and 2).

(2.4) The authors do not report some details about their ResNet18 design, specifically whether a global pooling layer is used and whether the output fully connected layer has any activation function. Additionally, they do not report the version of ResNet18 employed here, namely, whether the BatchNorm and ReLU are applied after (v1) or before (v2) the conv layers in the residual path.

We use ResNet18 v1 with no activation function nor bias in its last layer (this has been clarified in the lines 606-608). Also, by design, ResNet has a global average pool right before the last fully connected layer which we did not remove. In response to the reviewer, Resnet18 v2 was tested and its performance is the same as that of v1 (see Appendix 3—figure 1 and lines 590-591).

(3) Pair sampling strategy. The authors devised a clever approach for sampling positive and negative pairs that is tailored to the nature of the formulation. First, since the positive and negative labels are derived from the co-existence of pretracked fragments, selection has to be done at the level of fragments rather than individual images. This would not be the case if one of the newer approaches for contrastive learning were employed, but it serves as a strength here (assuming that fragment generation/first pass heuristic tracking is achievable and reliable in the dataset). Second, a clever weighted sampling scheme assigns sampling weights to the fragments that are designed to balance "exploration and exploitation". They weigh samples both by fragment length and by the loss associated with that fragment to bias towards different and more difficult examples.

(3.1) The formulation described here resembles and uses elements of online hard example mining (Shrivastava et al., 2016), hard negative sampling (Robinson et al., 2020\), and curriculum learning more broadly. The authors may consider referencing this literature (particularly Robinson et al., 2020\) for inspiration and to inform the interpretation of the current empirical results on positive/negative balancing.

Following this recommendation, we added references of hard negative mining in the new section “Differences with previous work in contrastive/metric learning”, lines 792-841. Regarding curriculum learning, even though in spirit it might have parallels with our sampling method in the sense that there is a guided training of the network, we believe the approach is more similar to an exploration-exploitation paradigm.

(4) Speed and accuracy improvements. The authors report considerable improvements in speed and accuracy of the new idTracker (v6) over the original idTracker (v4?) and TRex. It's a bit unclear, however, which of these are attributable to the engineering optimizations (v5?) versus the representation learning formulation.

(4.1) Why is there an improvement in accuracy in idTracker v5 (L77-81)? This is described as a port to PyTorch and improvements largely related to the memory and data loading efficiency. This is particularly notable given that the progression went from 97.52% (v4; original) to 99.58% (v5; engineering enhancements) to 99.92% (v6; representation learning), i.e., most of the new improvement in accuracy owes to the "optimizations" which are not the central emphasis of the systematic evaluations reported in this paper.

V5 was a two year-effort designed to improve time efficiency of v4. It was also a surprise to us that accuracy was higher, but that likely comes from the fact that the substituted code from v4 contained some small bug/s. The improvements in v5 are retained in v6 (contrastive learning) and v6 has higher accuracy and shorter tracking times. The difference in v6 for this extra accuracy and shorter tracking times is contrastive learning.

(4.2) What about the speed improvements? Relative to the original (v4), the authors report average speed-ups of 13.6x in v5 and 44x in v6. Presumably, the drastic speed-up in v6 comes from a lower Protocol 2 failure rate, but v6 is not evaluated in Figure 2 - figure supplement 2.

Idtracker.ai v5 runs an optimized Protocol 2 and, sometimes, the Protocol 3. But v6 doesn’t run either of them. While P2 is still present in v6 as a fallback protocol when contrastive fails, in our v6 benchmark P2 was never needed. So the v6 speedup comes from replacing both P2 and P3 with the contrastive algorithm.

(5) Robustness to occlusion. A major innovation enabled by the contrastive representation learning approach is the ability to tolerate the absence of a global fragment (contiguous frames where all animals are visible) by requiring only co-existing pairs of fragments owing to the paired sampling formulation. While this removes a major limitation of the previous versions of idtracker.ai, its evaluation could be strengthened. The authors describe an ablation experiment where an arc of the arena is masked out to assess the accuracy under artificially difficult conditions. They find that the v6 works robustly up to significant proportions of occlusions, even when doing so eliminates global fragments.

(5.1) The experiment setup needs to be more carefully described.

(5.1.1) What does the masking procedure entail? Are the pixels masked out in the original video or are detections removed after segmentation and first pass tracking is done?

The mask is defined as a region of interest in the software. This means that it is applied at the segmentation step where the video frame is converted to a foreground-background binary image. The region of interest is applied here, converting to background all pixels not inside of it. We clarified this in the newly added section Occlusion tests, lines 240-244.

(5.1.2) What happens at the boundary of the mask? (Partial segmentation masks would throw off the centroids, and doing it after original segmentation does not realistically model the conditions of entering an occlusion area.)

Animals at the boundaries of the mask are partially detected. This can change the location of their detected centroid. That’s why, when computing the ground-truth accuracy for these videos, only the groundtruth centroids that were at minimum 15 pixels further from the mask were considered. We clarified this in the newly added section Occlusion tests, lines 248-251.

(5.1.3) Are fragments still linked for animals that enter and then exit the mask area?

No artificial fragment linking was added in these videos. Detected fragments are linked the usual way. If one animal hides into the mask, the animal disappears so the fragment breaks.  We clarified this in the newly added section Occlusion tests, lines 245-247.

(5.1.4) How is the evaluation done? Is it computed with or without the masked region detections?

The groundtruth used to validate these videos contains the positions of all animals at all times. But only the positions outside the mask at each frame were considered to compute the tracking accuracy. We clarified this in the newly added section Occlusion tests, lines 248-251.

(5.2) The circular masking is perhaps not the most appropriate for the mouse data, which is collected in a rectangular arena.

We wanted to show the same proof of concept in different videos. For that reason, we used to cover the arena parametrized by an angle. In the rectangular arena the circular masking uses an external circle, so it is covering the rectangle parametrized by an angle.

(5.3) The number of co-existing fragments, which seems to be the main determinant of performance that the authors derive from this experiment, should be reported for these experiments. In particular, a "number of co-existing fragments" vs accuracy plot would support the use of the 0.25(N-1) heuristic and would be especially informative for users seeking to optimize experimental and cage design. Additionally, the number of co-existing fragments can be artificially reduced in other ways other than a fixed occlusion, including random dropout, which would disambiguate it from potential allocentric positional confounds (particularly relevant in arenas where egocentric pose is correlated with allocentric position).

We included the requested analysis about the fragment connectivity in Figure 3-figure supplement 1. We agree that there can be additional ways of reducing co-existing fragments, but we think the occlusion tests have the additional value that there are many real experiments similar to this test.

(6) Robustness to imaging conditions. The authors state that "the new idtracker.ai can work well with lower resolutions, blur and video compression, and with inhomogeneous light (Figure 2 - figure supplement 4)." (L156). Despite this claim, there are no speed or accuracy results reported for the artificially corrupted data, only examples of these image manipulations in the supplementary figure.

We added this information in the same image, new Figure 1 - figure supplement 3.

(7) Robustness across longitudinal or multi-session experiments. The authors reference idmatcher.ai as a compatible tool for this use case (matching identities across sessions or long-term monitoring across chunked videos), however, no performance data is presented to support its usage. This is relevant as the innovations described here may interact with this setting. While deep metric learning and contrastive learning for ReID were originally motivated by these types of problems (especially individuals leaving and entering the FOV), it is not clear that the current formulation is ideally suited for this use case. Namely, the design decisions described in point 1 of this review are at times at odds with the idea of learning generalizable representations owing to the feature extractor backbone (less scalable), low-dimensional embedding size (less representational capacity), and Euclidean distance metric without hypersphere embedding (possible sensitivity to drift). It's possible that data to support point 6 can mitigate these concerns through empirical results on variations in illumination, but a stronger experiment would be to artificially split up a longer video into shorter segments and evaluate how generalizable and stable the representations learned in one segment are across contiguous ("longitudinal") or discontiguous ("multi-session") segments.

We have now added a test to prove the reliability of idmatcher.ai in v6. In this test, 14 videos are taken from the benchmark and split in two non-overlapping parts (with a 200 frames gap in between). idmatcher.ai is run between the two parts presenting a 100% accuracy identity matching across all of them (see section “Validity of idmatcher.ai in the new idtracker.ai”, lines 969-1008).

We thank the reviewer for the detailed suggestions. We believe we have taken all of them into consideration to improve the ms.

Reviewer #3 (Public review):

Summary

The authors propose a new version of idTracker.ai for animal tracking. Specifically, they apply contrastive learning to embed cropped images of animals into a feature space where clusters correspond to individual animal identities.

Strengths

By doing this, the new software alleviates the requirement for so-called global fragments - segments of the video, in which all entities are visible/detected at the same time - which was necessary in the previous version of the method. In general, the new method reduces the tracking time compared to the previous versions, while also increasing the average accuracy of assigning the identity labels.

Weaknesses

The general impression of the paper is that, in its current form, it is difficult to disentangle the old from the new method and understand the method in detail. The manuscript would benefit from a major reorganization and rewriting of its parts. There are also certain concerns about the accuracy metric and reducing the computational time.

We have made the following modifications in the presentation:

(1) We have added section tiles to the main text so it is clearer what tracking system we are referring to. For example, we now have sections “Limitation of the original idtracker.ai”, “Optimizing idtracker.ai without changes in the learning method” and “The new idtracker.ai uses representation learning”.

(2) We have completely rewritten all the text of the ms until we start with contrastive learning. Old L20-89 is now L20-L66, much shorter and easier to read.

(3) We have rewritten the first 3 paragraphs in the section “The new idtracker.ai uses representation learning” (lines 68-92).

(4) We now expanded Appendix 3 to discuss the details of our approach  (lines 539-897).  It discusses in detail the steps of the algorithm, the network architecture, the loss function, the sampling strategy, the clustering and identity assignment, and the stopping criteria in training

(5) To cite previous work in detail and explain what we do differently, we have now added in Appendix 3 the new section “Differences with previous work in contrastive/metric learning” (lines 792-841).

Regarding accuracy metrics, we have replaced our accuracy metric with the standard metric IDF1. IDF1 is the standard metric that is applied to systems in which the goal is to maintain consistent identities across time. See also the section in Appendix 1 "Computation of tracking accuracy” (lines 414-436) explaining IDF1 and why this is an appropriate metric for our goal.

Using IDF1 we obtain slightly higher accuracies for the idtracker.ai systems. This is the comparison of mean accuracy over all our benchmark for our previous accuracy score and the new one for the full trajectories:

v4:   97.42% -> 98.24%

v5:   99.41% -> 99.49%

v6:   99.74% -> 99.82%

trex: 97.89% -> 97.89%

We thank the reviewer for the suggestions about presentation and about the use of more standard metrics.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Figure 1a: A graphical legend inset would make it more readable since there are multiple colors, line styles, and connecting lines to parse out.

Following this recommendation, we added a graphical legend in the old Figure 1 (new Figure 2).

(2) L46: "have images" → "has images".

We applied this correction. Line 35.

(3) L52: "videos start with a letter for the species (z,**f**,m)", but "d" is used for fly videos.

We applied this correction in the caption of Figure 1.

(4) L62: "with Protocol 3 a two-step process" → "with Protocol 3 being a two-step process".

We rewrote this paragraph without mentioning Protocol 3, lines 37-41.

(5) L82-89: This is the main statement of the problems that are being addressed here (speed and relaxing the need for global fragments). This could be moved up, emphasized, and made clearer without the long preamble and results on the engineering optimizations in v5. This lack of linearity in the narrative is also evident in the fact that after Figure 1a is cited, inline citations skip to Figure 2 before returning to Figure 1 once the contrastive learning is introduced.

We have rewritten all the text until the contrastive learning, (old lines 20-89 are now lines 20-66). The text is shorter, more linear and easier to read.

(6) L114: "pairs until the distance D_{pos}" → "pairs until the distance approximates D_{pos}".

We rewrote as “ pairs until the distance 𝐷pos (or 𝐷neg) is reached” in line 107.

(7) L570: Missing a right parenthesis in the equation.

We no longer have this equation in the ms.

(8) L705: "In order to identify fragments we, not only need" → "In order to identify fragments, we not only need".

We applied this correction, Line 775.

(9) L819: "probably distribution" → "probability distribution".

We applied this correction, Line 776.

(10) L833: "produced the best decrease the time required" → "produced the best decrease of the time required".

We applied this correction, Line 746.

Reviewer #3 (Recommendations for the authors):

(1) We recommend rewriting and restructuring the manuscript. The paper includes a detailed explanation of the previous approaches (idTracker and idTracker.ai) and their limitations. In contrast, the description of the proposed method is short and unstructured, which makes it difficult to distinguish between the old and new methods as well as to understand the proposed method in general. Here are a few examples illustrating the problem. 

(1.1) Only in line 90 do the authors start to describe the work done in this manuscript. The previous 3 pages list limitations of the original method.

We have now divided the main text into sections, so it is clearer what is the previous method (“Limitation of the original idtracker.ai”, lines 28-51), the new optimization we did of this method (“Optimizing idtracker.ai without changes in the learning method”, lines 52-66) and the new contrastive approach that also includes the optimizations (“The new idtracker.ai uses representation learning”, lines 66-164). Also, the new text has now been streamlined until the contrastive section, following your suggestion. You can see that in the new writing the three sections are 25 , 15 and 99 lines. The more detailed section is the new system, the other two are needed as reference, to describe which problem we are solving and the extra new optimizations.  

(1.2) The new method does not have a distinct name, and it is hard to follow which idtracker.ai is a specific part of the text referring to. Not naming the new method makes it difficult to understand.

We use the name new idtracker.ai (v6) so it becomes the current default version. v5 is now obsolete, as well as v4. And from the point of view of the end user, no new name is needed since v6 is just an evolution of the same software they have been using. Also, we added sections in the main text to clarify the ideas in there and indicate the version of idtracker.ai we are referring to.

(1.3) There are "Protocol 2" and "Protocol 3" mixed with various versions of the software scattered throughout the text, which makes it hard to follow. There should be some systematic naming of approaches and a listing of results introduced.

Following this recommendation we no longer talk about the specific protocols of the old version of idtracker.ai in the main text. We rewritten the explanation of these versions in a more clear and straightforward way, lines 29-36.

(2) To this end, the authors leave some important concepts either underexplained or only referenced indirectly via prior work. For example, the explanation of how the fragments are created (line 15) is only explained by the "video structure" and the algorithm that is responsible for resolving the identities during crossings is not detailed (see lines 46-47, 149-150). Including summaries of these elements would improve the paper's clarity and accessibility.

We listed the specific sections from our previous publication where the reader can find information about the entire tracking pipeline (lines 539-549). This way, we keep the ms clear and focused on the new identification algorithm while indicating where to find such information.

(3) Accuracy metrics are not clear. In line 319, the authors define it as based on "proportion of errors in the trajectory". This proportion is not explained. How is the error calculated if a trajectory is lost or there are identity swaps? Multi-object tracking has a range of accuracy metrics that account for such events but none of those are used by the authors. Estimating metrics that are common for MOT literature, for example, IDF1, MOTA, and MOTP, would allow for better method performance understanding and comparison.

In the new ms, we replaced our accuracy metric with the standard metric IDF1. IDF1 is the standard metric that is applied to systems in which the goal is to maintain consistent identities across time. See also the section in Appendix 1 "Computation of tracking accuracy” explaining why IDF1 and not MOTA or MOTP is the adequate metric for a system that wants to give correct tracking by identification in time. See lines 416-436.

Using IDF1 we obtain slightly higher accuracies for the idtracker.ai systems. This is the comparison of mean accuracy four our previous accuracy and the new one for the full trajectories:

v4:   97.42% -> 98.24%

v5:   99.41% -> 99.49%

v6:   99.74% -> 99.82%

trex: 97.89% -> 97.89%

(4) Additionally, the authors distinguish between tracking with and without crossings, but do not provide statistics on the frequency of crossings per video. It is also unclear how the crossings are considered for the final output. Including information such as the frame rate of the videos would help to better understand the temporal resolution and the differences between consecutive frames of the videos.

We added this information in the Appendix 1 “Benchmark of accuracy and tracking time”, lines 445-451. The framerate in our benchmark videos goes from 25 to 60 fps (average of 37 fps). On average 2.6% of the blobs are crossings (1.1% for zebrafish 0.7% for drosophila 9.4% for mice).

(5) In the description of the dataset used for evaluation (lines 349-365), the authors describe the random sampling of parameter values for each tracking run. However, it is unclear whether the same values were used across methods. Without this clarification, comparisons between the proposed method, older versions, and TRex might be biased due to lucky parameter combinations. In addition, the ranges from which the values were randomly sampled were also not described.

Only one parameter is shared between idtracker.ai and TRex: intensity_threshold (in idtracker.ai) and threshold (in TRex). Both are conceptually equivalent but differ in their numerical values since they affect different algorithms. V4, v5, and TRex each required the same process of independent expert visual inspection of the segmentation to select the valid value range. Since versions 5 and 6 use exactly the same segmentation algorithm, they share the same parameter ranges.

All the ranges of valid values used in our benchmark are public here https://drive.google.com/drive/folders/1tFxdtFUudl02ICS99vYKrZLeF28TiYpZ as stated in the section “Data availability”, lines 227-228.

(6) Lines 122-123, Figure 1c. "batches" - is an imprecise metric of training time as there is no information about the batch size.

We clarified the Figure caption, new Figure 2c.

(7) Line 145 - "we run some steps... For example..." leaves the method description somewhat unclear. It would help if you could provide more details about how the assignments are carried out and which metrics are being used.

Following this recommendation, we listed the specific sections from our previous publication where the reader can find information about the entire tracking pipeline (lines 539-549). This way, we keep the ms clear and focused on the new identification algorithm while indicating where to find such information.

(8) Figure 3. How is tracking accuracy assessed with occlusions? Are the individuals correctly recognized when they reappear from the occluded area?

The groundtruth for this video contains the positions of all animals at all times. Only the groundtruth points inside the region of interest are taken into account when computing the accuracy. When the tracking reaches high accuracy, it means that animals are successfully relabeled every time they enter the non-masked region. Note that this software works all the time by identification of animals, so crossings and occlusion are treated the same way. What is new here is that the occlusions are so large that there are no global fragments. We clarified this in the new section “Occlusion tests” in Methods, lines 239-251.

(9) Lines 185-187 this part of the sentence is not clear.

We rewrote this part in a clearer way, lines 180-182.

(10) The authors also highlight the improved runtime performance. However, they do not provide a detailed breakdown of the time spent on each component of the tracking/training pipeline. A timing breakdown would help to compare the training duration with the other components. For example, the calculation of the Silhouette Score alone can be time-consuming and could be a bottleneck in the training process. Including this information would provide a clearer picture of the overall efficiency of the method.

We measured that the training of ResNet takes on average in our benchmark 47% of the tracking time (we added this information line 551 section “Network Architecture”). In this training stage the bottleneck becomes the network forward and backward pass, limited by the GPU performance. All other processes happening during training have been deeply optimized and parallelized when needed so their contribution to the training time is minimal. Apart from the training, we also measured 24.4% of the total tracking time spent in reading and segmenting the video files and 11.1% in processing the identification images and detecting crossings.

(11) An important part of the computational cost is related to model training. It would be interesting to test whether a model trained on one video of a specific animal type (e.g., zebrafish_5) generalizes to another video of the same type (e.g., zebrafish_7). This would assess the model's generalizability across different videos of the same species and spare a lot of compute. Alternatively, instead of training a model from scratch for each video, the authors could also consider training a base model on a superset of images from different videos and then fine-tuning it with a lower learning rate for each specific video. This could potentially save time and resources while still achieving good performance.

Already before v6, there was the possibility for the user to start training the identification network by copying the final weights from another tracking session. This knowledge transfer feature is still present in v6 and it still decreases the training times significatively. This information has been added in Appendix 4, lines 906-909.

We have already begun working on the interesting idea of a general base model but it brings some complex challenges. It could be a very useful new feature for future idtracker.ai releases.

We thank the reviewer for the many suggestions. We have implemented all of them.

Author response:

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

Public Reviews:

Reviewer #2 (Public review):

(1) Vglut2 isn't a very selective promoter for the STN. Did the authors verify every injection across brain slices to ensure the para-subthalamic nucleus, thalamus, lateral hypothalamus, and other Vglut2-positive structures were never infected?

The STN is anatomically well-confined, with its borders and the overlying zona incerta (composed of GABAergic neurons) providing protection against off-target expression in most neighboring forebrain regions. All viral injections were histologically verified and did not into extend into thalamic or hypothalamic areas. As described in the Methods, we employed an app we developed (Brain Atlas Analyzer, available on OriginLab) that aligns serial histological sections with the Allen Brain Atlas to precisely assess viral spread and confirm targeting accuracy. The experiments included in the revised manuscript now focus on optogenetic inhibition and irreversible lesion approaches—three complementary methods that consistently targeted the STN and yielded similar behavioral effects.

(2) The authors say in the methods that the high vs low power laser activation for optogenetic experiments was defined by the behavioral output. This is misleading, and the high vs low power should be objectively stated and the behavioral results divided according to the power used, not according to the behavioral outcome.

Optogenetic excitation is no longer part of the study.

(3) In the fiber photometry experiments exposing mice to the range of tones, it is impossible to separate the STN response to the tone from the STN response to the movement evoked by the tone. The authors should expose the mouse to the tones in a condition that prevents movement, such as anesthetized or restrained, to separate out the two components.

The new mixed-effects modeling approach clearly differentiates sensory (auditory) from motor contributions during tone-evoked STN activation. In prior work (see Hormigo et al, 2023, eLife), we explored experimental methods such as head restraint or anesthesia to reduce movement, but we concluded that these approaches are unsuitable for addressing this question. Mice exhibit substantial residual movement even when head-fixed, and anesthesia profoundly alters neural excitability and behavioral state, introducing major confounds. To fully eliminate movement would require paralysis and artificial ventilation, which would again disrupt physiological network dynamics and raise ethical concerns. Therefore, the current modeling approach—incorporating window-specific covariates for movement—is the most appropriate and rigorous way to dissociate tone-evoked sensory activity from motor activity in behaving animals.

(4) The claim 'STN activation is ideally suited to drive active avoids' needs more explanation. This claim comes after the fiber photometry experiments during active avoidance tasks, so there has been no causality established yet.

Text adjusted. 

(5) The statistical comparisons in Figure 7E need some justification and/or clarification. The 9 neuron types are originally categorized based on their response during avoids, then statistics are run showing that they respond differently during avoids. It is no surprise that they would have significantly different responses, since that is how they were classified in the first place. The authors must explain this further and show that this is not a case of circular reasoning.

Statistically verifying the clustering is useful to ensure that the selected number of clusters reflects distinct classes. It is also necessary when different measurements are used to classify (movement time series classified the avoids) and to compare neuronal types within each avoid mode/class (know called “mode”). Moreover, the new modeling approach goes beyond the prior statistical limitations related to considering movement and neuronal variables separately. 

(6) The authors show that neurons that have strong responses to orientation show reduced activity during avoidance. What are the implications of this? The author should explain why this is interesting and important.

The new modeling approach goes beyond the prior analysis limitations. For instance, it shows that most of the prior orienting related activations closely reflect the orienting movement, and only in a few cases (noted and discussed in the results) orienting activations are related to the behavioral contingencies or behavioral outcomes in the task. 

(8) The experiments in Figure 10 are used to say that STN stimulation is not aversive, but they only show that STN stimulation cannot be used as punishment in place of a shock. This doesn't mean that it is not aversive; it just means it is not as aversive as a shock. The authors should do a simpler aversion test, such as conditioned or real-time place preference, to claim that STN stimulation is not aversive. This is particularly surprising as previous work (Serra et al., 2023) does show that STN stimulation is aversive.

Optogenetic excitation is no longer part of the study. 

(7) It is not clear which conditions each mouse experienced in which order. This is critical to the interpretation of Figure 9 and the reduction of passive avoids during STN stimulation. Did these mice have the CS1+STN stimulation pairing or the STN+US pairing prior to this experiment? If they did, the stimulation of the STN could be strongly associated with either punishment or with the CS1 that predicts punishment. If that is the case, stimulating the STN during CS2 could be like presenting CS1+CS2 at the same time and could be confusing.

Optogenetic excitation is no longer part of the study. 

(8) The experiments in Figure 10 are used to say that STN stimulation is not aversive, but they only show that STN stimulation cannot be used as punishment in place of a shock. This doesn't mean that it is not aversive; it just means it is not as aversive as a shock. The authors should do a simpler aversion test, such as conditioned or real-time place preference, to claim that STN stimulation is not aversive. This is particularly surprising as previous work (Serra et al., 2023) does show that STN stimulation is aversive.

Optogenetic excitation is no longer part of the study.

(9) In the discussion, the idea that the STN encodes 'moving away' from contralateral space is pretty vague and unsupported. It is puzzling that the STN activates more strongly to contraversive turns, but when stimulated, it evokes ipsiversive turns; however, it seems a stretch to speculate that this is related to avoidance. In the last experiments of the paper, the axons from the STN to the GPe and to the midbrain are selectively stimulated. Do these evoke ipsiversive turns similarly?

Optogenetic excitation is no longer part of the study. 

(10) In the discussion, the authors claim that the STN is essential for modulating action timing in response to demands, but their data really only show this in one direction. The STN stimulation reliably increases the speed of response in all conditions (except maximum speed conditions such as escapes). It seems to be over-interpreting the data to say this is an inability to modulate the speed of the task, especially as clear learning and speed modulation do occur under STN lesion conditions, as shown in Figure 12B. The mice learn to avoid and increase their latency in AA2 vs AA1, though the overall avoids and latency are different from controls. The more parsimonious conclusion would be that STN stimulation biases movement speed (increasing it) and that this is true in many different conditions.

Optogenetic excitation is no longer part of the study.

(11)  In the discussion, the authors claim that the STN projections to the midbrain tegmentum directly affect the active avoidance behavior, while the STN projections to the SNr do not affect it. This seems counter to their results, which show STN projections to either area can alter active avoidance behavior. What is the laser power used in these terminal experiments? If it is high (3mW), the authors may be causing antidromic action potentials in the STN somas, resulting in glutamate release in many brain areas, even when terminals are only stimulated in one area. The authors could use low (0.25mW) laser power in the terminals to reduce the chance of antidromic activation and spatially restrict the optical stimulation.

Optogenetic excitation is no longer part of the study. 

(12) Was normality tested for data prior to statistical testing?

Yes, although now we use mixed models

(13) Why are there no error bars on Figure 5B, black circles and orange triangles?

When error bars are not visible, they are smaller than the trace thickness or bar line—for example, in Figure 5B, the black circles and orange triangles include error bars, but they are smaller than the symbol size.

Reviewer #3 (Public review):

(1) I really don't understand or accept this idea that delayed movement is necessarily indicative of cautious movements. Is the distribution of responses multi-modal in a way that might support this idea, or do the authors simply take a normal distribution and assert that the slower responses represent 'caution'? Even if responses are multi-modal and clearly distinguished by 'type', why should readers think this that delayed responses imply cautious responding instead of say: habituation or sensitization to cue/shock, variability in attention, motivation, or stress; or merely uncertainty which seems plausible given what I understand of the task design where the same mice are repeatedly tested in changing conditions. This relates to a major claim (i.e., in the work's title).

In our study, “caution” is defined operationally as the tendency to delay initiation of an avoidance response in demanding situations (e.g., taking more time or care before crossing a busy street). The increase in avoidance latency with task difficulty is highly robust, as we have shown previously through detailed analyses of timing distributions and direct comparisons with appetitive behaviors (e.g., Zhou et al., 2022 JNeurosci). Moreover, we used the tracked movement time series to statistically classify responses into cautious modes, which is likely novel. This definition can dissociate cautious responding from broader constructs listed by a reviewer, such as attention, motivation, or stress, which must be explicitly defined to be rigorously considered in this context, including the likelihood that they covary with caution without being equivalent to it. 

Cue-evoked orienting responses at CS onset are directly measured, and their habituation and sensitization have been characterized in our prior work (e.g., Zhou et al., 2023 JNeurosci). US-evoked escapes are also measured in the present study and directly compared with avoidance responses. Together, these analyses provide a rigorous and consistent framework for defining and quantifying caution within our behavioral procedures.

Importantly, mice exhibit cautious responding as defined here across different tasks, making it more informative to classify avoidance responses by behavioral mode rather than by task alone. Accordingly, in the miniscope, single-neuron, and mixed-effects model analyses, we classified active avoids into distinct modes reflecting varying levels of caution. Although these modes covary with task contingencies, their explicit classification improves model predictability and interpretability with respect to cautious responding.

(2) Related to the last, I'm struggling to understand the rationale for dividing cells into 'types' based the their physiological responses in some experiments (e.g., Figure 7).

This section has now been expanded into 3 figures (Fig. 7-9) with new modeling approaches that should make the rationale more straight forward.

By emphasizing the mixed-effects modeling results and integrating these analyses directly into the figures, the revised manuscript now more clearly delineates what is encoded at the population and single-neuron levels. Including movement and baseline covariates allowed us to dissociate motor-related modulation from other neural signals, substantially clarifying the distinction between movement encoding and other task-related variables, which we focus on in the paper. These analyses confirm the strong role of the STN in representing movement while revealing additional signals related to aversive stimulation and cautious responding that persist after accounting for motor effects. These signals arise from distinct neuronal populations that can be differentiated by their movement sensitivity and activation patterns across avoidance modes, reflecting varying levels of caution. At the same time, several effects that initially reflected orienting-related activity at CS-onset (note that our movement tracking captures both head position and orientation as a directional vector) dissipated once movement and baseline covariates were included in the models, emphasizing the utility of the analytical improvements in the revision.

(3)The description and discussion of orienting head movements were not well supported, but were much discussed in the avoidance datasets. The initial speed peaks to cue seem to be the supporting data upon which these claims rest, but nothing here suggests head movement or orientation responses.

As described in the methods (and noted above), we track the head and decompose the movement into rotational and translational components. With the new approach, several effects that initially reflected orienting-related activity at CS-onset (note that our movement tracking captures both head position and orientation as a directional vector) dissipated once movement and baseline covariates were included in the models, emphasizing the utility of the analytical improvements in the revision.

(4) Similar to the last, the authors note in several places, including abstract, the importance of STN in response timing, i.e., particularly when there must be careful or precise timing, but I don't think their data or task design provides a strong basis for this claim.

The avoidance modes and the measured latencies directly support the relation to action timing, but now the portion of the previous paper about optogenetic excitation and apparently the main source of criticism is no longer in the present study. 

(5) I think that other reports show that STN calcium activity is recruited by inescapable foot shock as well. What do these authors see? Is shock, independent of movement, contributing to sharp signals during escapes?

The question, “Is shock, independent of movement, contributing to sharp signals during escapes?” is now directly addressed in the revised analyses. By incorporating movement and baseline covariates into the mixed-effects models, we dissociate STN activity related to aversive stimulation from that associated with motor output. The results show that shock-evoked STN activation persists even after controlling for movement within defined neuronal populations, supporting a specific nociceptive contribution independent of motor dynamics—a dissociation that appears to be new in this field.

(6) In particular, and related to the last point, the following work is very relevant and should be cited:  Note that the focus of this other paper is on a subset of VGLUT2+ Tac1 neurons in paraSTN, but using VGLUT2-Cre to target STN will target both STN and paraSTN.

We appreciate the reviewer’s reference to the recent preprint highlighting the role of the para-subthalamic nucleus in avoidance learning. However, our study focused specifically on performance in well-trained mice rather than on learning processes. Behavioral learning is inherently more variable and can be disrupted by less specific manipulations, whereas our experiments targeted the stable execution of learned avoidance behaviors. Future work will extend these findings to the learning phase and examine potential contributions of subthalamic subdivisions, which our current Vglut2-based manipulations do not dissociate. We will consider this and related work more closely in those studies.

(7) In multiple other instances, claims that were more tangential to the main claims were made without clearly supporting data or statistics. E.g., claim that STN activation is related to translational more than rotational movement; claim that GCaMP and movement responses to auditory cues were small; claims that 'some animals' responded differently without showing individual data.

We have adjusted the text accordingly.

(8) In several figures, the number of subjects used was not described. This is necessary. Also necessary is some assessment of the variability across subjects. The only measure of error shown in many figures relates to trial-to-trial or event variability, which is minimal because, in many cases, it appears that hundreds of trials may have been averaged per animal, but this doesn't provide a strong view of biological variability. When bar/line plots are used to display data, I recommend showing individual animals where feasible.

All experiments report number of mice and sessions. Wherever feasible, we display individual data points (e.g., Figures 1 and 2) to convey variability directly. However, in cases where figures depict hundreds of paired (repeated-measures) data points, showing all points without connecting them would not be appropriate, while linking them would make the figures visually cluttered and uninterpretable. All plots and traces include measures of variability (SEM), and the raw data will be shared on Dryad. When error bars are not visible, they are smaller than the trace thickness or bar line—for example, in Figure 5B, the black circles and orange triangles include error bars, but they are smaller than the symbol size.

Also, to minimize visual clutter, only a subset of relevant comparisons is highlighted with asterisks, whereas all relevant statistical results, comparisons, and mouse/session numbers are fully reported in the Results section, with statistical analyses accounting for the clustering of data within subjects and sessions.

(9) Can the authors consider the extent to which calcium imaging may be better suited to identify increases compared to decreases and how this may affect the results, particularly related to the GRIN data when similar numbers of cells show responses in both directions (e.g., Figure 3)?

This is an interesting issue related to a widely used technique beyond the scope of our study.

(10) Raw example traces are not provided.

We do not think raw traces are useful here. All figures contain average traces to reflect the activity of the estimated population.

(11) The timeline of the spontaneous movement and avoidance sessions was not clear, nor was the number of events or sessions per animal nor how this was set. It is not clear if there was pre-training or habituation, if many or variable sessions were combined per animal, or what the time gaps between sessions were, or if or how any of these parameters might influence interpretation of the results.

We have enhanced the description of the sessions, including the number of animals and sessions, which are daily and always equal per animals in each group of experiments. As noted, the sessions are part of the random effects in the model.

(12) It is not clear if or how the spread of expression outside of the target STN was evaluated, and if or how many mice were excluded due to spread or fiber placements.

The STN is anatomically well-confined, with its borders and the overlying zona incerta (composed of GABAergic neurons) providing protection against off-target expression in most neighboring forebrain regions. All viral injections were histologically verified and did not into extend into thalamic or hypothalamic areas. As described in the Methods, we employed an app we developed (Brain Atlas Analyzer, available on OriginLab) that aligns serial histological sections with the Allen Brain Atlas to precisely assess viral spread and confirm targeting accuracy. The experiments included in the revised manuscript now focus on optogenetic inhibition and irreversible lesion approaches—three complementary methods that consistently targeted the STN and yielded similar behavioral effects.

Recommendations for the authors:

Reviewing Editor Comments:

The primary feedback agreed upon by all the reviewers was that the manuscript requires significant streamlining as it is currently overly long and convoluted.

We thank the reviewers and editors for their thoughtful and constructive feedback. In response to the primary comment that “the manuscript requires significant streamlining as it is currently overly long and convoluted,” we have substantially revised and refocused the paper. Specifically, we streamlined the included data and enhanced the analyses to emphasize the central findings: the encoding of movement, cautious responding, and punishment in the STN during avoidance behavior. We also focused the causal component of the study by including only the loss-of-function experiments—both optogenetic inhibition and irreversible viral/electrolytic lesions—that establish the critical role of STN circuits in generating active avoidance. Together, these revisions enhance clarity, tighten the narrative focus, and align the manuscript more closely with the reviewers’ recommendations.

Major revisions include the addition of mixed-effects modeling to dissociate the contributions of movement from other STN-encoded signals related to caution and punishment. This modeling approach allowed us to reveal that these components are statistically separable, demonstrating that movement, cautious responding, and aversive input are encoded by neuronal subsets. To streamline the manuscript and address reviewer concerns, we removed the optogenetic excitation experiments. As revised, the paper presents a more concise and cohesive narrative showing that STN neurons differentially encode movement, caution, and aversive stimuli, and that this circuitry is essential for generating active avoidance behavior.

Many of the specific points raised by reviewers now fall outside the scope of the revised manuscript. This is primarily because the revised version omits data and analyses related to optogenetic excitation and associated control experiments. By removing these components, the paper now presents a streamlined and internally consistent dataset focused on how the STN encodes movement, cautious responding, and aversive outcomes during avoidance behavior, as well as on loss-of-function experiments demonstrating its necessity for generating active avoidance. Below, we address the points that remain relevant across reviews.

Following extensive revisions, the current manuscript differs in several important ways from what the assessment describes:

The description that the study “uses fiber photometry, implantable lenses, and optogenetics” is more accurately represented as using both fiber photometry and singleneuron calcium imaging with miniscopes, combined with optogenetic and irreversible lesion approaches.

The phrase stating that “active but not passive avoidance depends in part on STN projections to substantia nigra” is better characterized as “STN projections to the midbrain,” since our data show that optogenetic inhibition of STN terminals in both the mesencephalic reticular tegmentum (MRT) and substantia nigra pars reticulata (SNr) produce equivalent effects, and thus these sites are combined in the study. 

Finally, the original concern that evidence for STN involvement in cautious responding or avoidance speed was incomplete no longer applies. The revised focus on encoding, through the inclusion of mixed-effects modeling, now dissociates movement-related, cautious, and aversive components of STN activity. By removing the optogenetic excitation data, we no longer claim that the STN controls caution but rather that it encodes cautious responding, alongside movement and punishment signals. Furthermore, loss-of-function experiments demonstrate that silencing STN output abolishes active avoidance entirely, supporting an essential role for the STN in generating goal-directed avoidance behavior—a behavioral domain that, unlike appetitive responding, is fundamentally defined by caution and the need to balance action timing under threat.

Reviewer #2 (Recommendations for the authors):

(1) Show individual data points on bar plots.

Wherever feasible, we display individual data points (e.g., Figures 1 and 2) to convey variability directly. However, in cases where figures depict hundreds of paired (repeatedmeasures) data points, showing all points without connecting them would not be appropriate, while linking them would make the figures visually cluttered and uninterpretable. All plots and traces include measures of variability (SEM), and the raw data will be shared on Dryad. When error bars are not visible, they are smaller than the trace thickness or bar line—for example, in Figure 5B, the black circles and orange triangles include error bars, but they are smaller than the symbol size.

Also, to minimize visual clutter, only a subset of relevant comparisons is highlighted with asterisks, whereas all relevant statistical results, comparisons, and mouse/session numbers are fully reported in the Results section, with statistical analyses accounting for the clustering of data within subjects and sessions.

(2) The active avoidance experiments are confusing when they are introduced in the results section. More explanation of what paradigms were used and what each CS means at the time these are introduced would add clarity. For example, AA1, AA2, etc, are explained only with references to other papers, but a brief description of each protocol and a schematic figure would really help.

The avoidance protocols (AA1–4) are now described briefly but clearly in the Results section (second paragraph of “STN neurons activate during goal-directed avoidance contingencies”) and in greater detail in the Methods section. As stated, these tasks were conducted sequentially, and mice underwent the same number of sessions per procedure, which are indicated. All relevant procedural information has been included in these sections. Mice underwent daily sessions and learnt these tasks within 1-2 sessions, progressing sequentially across tasks with an equal number of sessions per task (7 per task), and the resulting data were combined and clustered by mouse/session in the statistical models.

(3) How do the Class 1, 2, 3 avoids relate to Class 1, 2, 3 neural types established in Figure 3? It seems like they are not related, and if that is the case, they should be named something different from each other to avoid confusion. (4) Similarly, having 3 different cell types (a,b,c) in the active avoidance seems unrelated to the original classification of cell types (1,2,3), and these are different for each class of avoid. This is very confusing, and it is unclear how any of these types relate to each other. Presumably, the same mouse has all three classes of avoids, so there are recordings from each cell during each type of avoid.

The terms class, mode, and type are now clearly distinguished throughout the manuscript. Modes refer to distinct patterns of avoidance behavior that differ in the level of cautious responding (Mode 3 is most cautious). Within each mode, types denote subgroups of neurons identified based on their ΔF/F activity profiles. In contrast, classes categorize neurons according to their relationship to movement, determined by cross-correlation analyses between ΔF/F and head speed (Class1-4; Fig. 7 is a new analysis) or head turns (ClassA-C, renamed from 1-3). This updated terminology clarifies the analytic structure, highlighting distinct neuronal populations within each analysis. For example, during avoidance behaviors, these classifications distinguish neurons encoding movement-, caution-, and outcome-related signals. Comparisons are conducted within each analytical set, within classes (A-C or 1-4 separately), within avoidance modes, or within modespecific neuronal types.

…So the authors could compare one cell during each avoid and determine whether it relates to movement or sound, or something else. It is interesting that types a,b, and c have the exact same proportions in each class of avoid, and makes it important to investigate if these are the exact same cells or not.

That previous table with the a,b,c % in the three figure panels was a placeholder, which was not updated in the included figure. It has now been correctly updated. They do not have the same proportions as shown in Fig. 9, although they are similar.

Also, these mice could be recorded during the open field, so the original neural classification (class 1, 2,3) could be applied to these same cells, and then the authors can see whether each cell type defined in the open field has a different response to the different avoid types. As it stands, the paper simply finds that during movement and during avoidance behaviors, different cells in the STN do different things.

We included a new analysis in Fig. 7 that classifies neurons based on the cross-correlation with movement. The inclusion of the models now clearly assigns variance to movement versus the other factors, and this analysis leads to the classification based on avoid modes. 

(5) The use of the same colors to mean two different things in Figure 9 is confusing. AA1 vs AA2 shouldn't be the same colors as light-naïve vs light signaling CS.

Optogenetic excitation is no longer part of the study.

(6) The exact timeline of the optogenetics experiments should be presented as a schematic for understanding. It is not clear which conditions each mouse experienced in which order. This is critical to the interpretation of Figure 9 and the reduction of passive avoids during STN stimulation. Did these mice have the CS1+STN stimulation pairing or the STN+US pairing prior to this experiment? If they did, the stimulation of the STN could be strongly associated with either punishment or with the CS1that predicts punishment. If that is the case, stimulating the STN during CS2 could be like presentingCS1+CS2 at the same time and could be confusing. The authors should make it clear whether the mice were naïve during this passive avoid experiment or whether they had experienced STN stimulation paired with anything prior to this experiment.

Optogenetic excitation is no longer part of the study.

(20) Similarly, the duration of the STN stimulation should be made clear on the plots that show behavior over time (e.g., Figure 9E).

Optogenetic excitation is no longer part of the study.

(21) There is just so much data and so many conditions for each experiment here. The paper is dense and difficult to read. It would really benefit readability if the authors put only the key experiments and key figure panels in the main text and moved much of the repetitive figure panels to supplemental figures. The addition of schematic drawings for behavioral experiment timing and for the different AA1, AA2, and AA3 conditions would also really improve clarity.

By focusing the study, we believe it has substantially improved clarity and readability. 

Reviewer #3 (Recommendations for the authors):

(1) Minor error in results 'Cre-AAV in the STN of Vglut2-Cre' Fixed.

(2) In some Figure 2 panels, the peaks appear to be cut off, and blue traces are obscured by red.

In Fig. 2, the peaks of movement (speed) traces are intentionally truncated to emphasize the rising phase of the turn, which would otherwise be obscured if the full y-axis range were displayed (peaks and other measures are statistically compared). This adjustment enhances clarity without omitting essential detail and is now noted in the legend.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Artiushin et al. establish a comprehensive 3D atlas of the brain of the orb-web building spider Uloborus diversus. First, they use immunohistochemistry detection of synapsin to mark and reconstruct the neuropils of the brain of six specimens and they generate a standard brain by averaging these brains. Onto this standard 3D brain, they plot immunohistochemical stainings of major transmitters to detect cholinergic, serotonergic, octopaminergic/taryminergic and GABAergic neurons, respectively. Further, they add information on the expression of a number of neuropeptides (Proctolin, AllatostatinA, CCAP, and FMRFamide). Based on this data and 3D reconstructions, they extensively describe the morphology of the entire synganglion, the discernible neuropils, and their neurotransmitter/neuromodulator content.

Strengths:

While 3D reconstruction of spider brains and the detection of some neuroactive substances have been published before, this seems to be the most comprehensive analysis so far, both in terms of the number of substances tested and the ambition to analyze the entire synganglion. Interestingly, besides the previously described neuropils, they detect a novel brain structure, which they call the tonsillar neuropil.<br /> Immunohistochemistry, imaging, and 3D reconstruction are convincingly done, and the data are extensively visualized in figures, schemes, and very useful films, which allow the reader to work with the data. Due to its comprehensiveness, this dataset will be a valuable reference for researchers working on spider brains or on the evolution of arthropod brains.

Weaknesses:

As expected for such a descriptive groundwork, new insights or hypotheses are limited, apart from the first description of the tonsillar neuropil. A more comprehensive labeling in the panels of the mentioned structures would help to follow the descriptions. The reconstruction of the main tracts of the brain would be a very valuable complementary piece of data.

Reviewer #2 (Public review):

Summary

Artiushin et al. created the first three-dimensional atlas of a synganglion in the hackled orb-weaver spider, which is becoming a popular model for web-building behavior. Immunohistochemical analysis with an impressive array of antisera reveals subcompartments of neuroanatomical structures described in other spider species as well as two previously undescribed arachnid structures, the protocerebral bridge, hagstone, and paired tonsillar neuropils. The authors describe the spider's neuroanatomy in detail and discuss similarities and differences from other spider species. The final section of the discussion examines the homology between onychophoran and chelicerate arcuate bodies and mandibulate central bodies.

Strengths

The authors set out to create a detailed 3D atlas and accomplished this goal.

Exceptional tissue clearing and imaging of the nervous system reveal the three-dimensional relationships between neuropils and some connectivity that would not be apparent in sectioned brains.

A detailed anatomical description makes it easy to reference structures described between the text and figures.

The authors used a large palette of antisera which may be investigated in future studies for function in the spider nervous system and may be compared across species.

Weaknesses

It would be useful for non-specialists if the authors would introduce each neuropil with some orientation about its function or what kind of input/output it receives, if this is known for other species. Especially those structures that are not described in other arthropods, like the opisthosomal neuropil. Are there implications for neuroanatomical findings in this paper on the understanding of how web-building behaviors are mediated by the brain?

Likewise, where possible, it would be helpful to have some discussion of the implications of certain neurotransmitters/neuropeptides being enriched in different areas. For example, GABA would signal areas of inhibitory connections, such as inhibitory input to mushroom bodies, as described in other arthropods. In the discussion section on relationships between spider and insect midline neuropils, are there similarities in expression patterns between those described here and in insects?

Reviewer #3 (Public review):

Summary:

This is an impressive paper that offers a much-needed 3D standardized brain atlas for the hackled-orb weaving spider Uloborus diversus, an emerging organism of study in neuroethology. The authors used a detailed immunohistological whole-mount staining method that allowed them to localize a wide range of common neurotransmitters and neuropeptides and map them on a common brain atlas. Through this approach, they discovered groups of cells that may form parts of neuropils that had not previously been described, such as the 'tonsillar neuropil', which might be part of a larger insect-like central complex. Further, this work provides unique insights into the previously underappreciated complexity of higher-order neuropils in spiders, particularly the arcuate body, and hints at a potentially important role for the mushroom bodies in vibratory processing for web-building spiders.

Strengths:

To understand brain function, data from many experiments on brain structure must be compiled to serve as a reference and foundation for future work. As demonstrated by the overwhelming success in genetically tractable laboratory animals, 3D standardized brain atlases are invaluable tools - especially as increasing amounts of data are obtained at the gross morphological, synaptic, and genetic levels, and as functional data from electrophysiology and imaging are integrated. Among 'non-model' organisms, such approaches have included global silver staining and confocal microscopy, MRI, and, more recently, micro-computed tomography (X-ray) scans used to image multiple brains and average them into a composite reference. In this study, the authors used synapsin immunoreactivity to generate an averaged spider brain as a scaffold for mapping immunoreactivity to other neuromodulators. Using this framework, they describe many previously known spider brain structures and also identify some previously undescribed regions. They argue that the arcuate body - a midline neuropil thought to have diverged evolutionarily from the insect central complex - shows structural similarities that may support its role in path integration and navigation.

Having diverged from insects such as the fruit fly Drosophila melanogaster over 400 million years ago, spiders are an important group for study - particularly due to their elegant web-building behavior, which is thought to have contributed to their remarkable evolutionary success. How such exquisitely complex behavior is supported by a relatively small brain remains unclear. A rich tradition of spider neuroanatomy emerged in the previous century through the work of comparative zoologists, who used reduced silver and Golgi stains to reveal remarkable detail about gross neuroanatomy. Yet, these techniques cannot uncover the brain's neurochemical landscape, highlighting the need for more modern approaches-such as those employed in the present study.

A key insight from this study involves two prominent higher-order neuropils of the protocerebrum: the arcuate body and the mushroom bodies. The authors show that the arcuate body has a more complex structure and lamination than previously recognized, suggesting it is insect central complex-like and may support functions such as path integration and navigation, which are critical during web building. They also report strong synapsin immunoreactivity in the mushroom bodies and speculate that these structures contribute to vibratory processing during sensory feedback, particularly in the context of web building and prey localization. These findings align with prior work that noted the complex architecture of both neuropils in spiders and their resemblance (and in some cases greater complexity) compared to their insect counterparts. Additionally, the authors describe previously unrecognized neuropils, such as the 'tonsillar neuropil,' whose function remains unknown but may belong to a larger central complex. The diverse patterns of neuromodulator immunoreactivity further suggest that plasticity plays a substantial role in central circuits.

Weaknesses:

My major concern, however, is that some of the authors' neuroanatomical descriptions rely too heavily on inference rather than what is currently resolvable from their immunohistochemistry stains alone.

We would like to thank the reviewers for their time and effort in carefully reading our manuscript and providing helpful feedback, and particularly for their appreciation and realistic understanding of the scope of this study and its context within the existing spider neuroanatomical literature.

Regarding the limitations and potential additions to this study, we believe these to be well-reasoned and are in agreement. We plan to address some of these shortcomings in future publications.

As multiple reviewers remarked, a mapping of the major tracts of the brain would be a welcome addition to understanding the neuroanatomy of U. diversus. This is something which we are actively working on and hope to provide in a forthcoming publication. Given the length of this paper as is, we considered that a treatment of the tracts would be better served as an additional paper. Likewise, mapping of the immunoreactive somata of the currently investigated targets is a component which we would like to describe as part of a separate paper, keeping the focus of the current one on neuropils, in order to leverage our aligned volumes to describe co-expression patterns, which is not as useful for the more widely dispersed somata. Furthermore, while we often see somata through immunostaining, the presence and intensity of the signal is variable among immunoreactive populations. We are finding that these populations are more consistently and comprehensively revealed thru fluorescent in situ hybridization.

We appreciate the desire of the reviewers for further information regarding the connectivity and function of the described neuropils, and where possible we have added additional statements and references. That being said, where this context remains sparse is largely a reflection of the lack of information in the literature. This is particularly the case for functional roles for spider neuropils, especially higher order ones of the protocerebrum, which are essentially unexamined. As summarized in the quite recent update to Foelix’s Spider Neuroanatomy, a functional understanding for protocerebral neuropil is really only available for the visual pathway. Consequently, it is therefore also difficult to speak of the implications for presence or absence of particular signaling elements in these neuropils, if no further information about the circuitry or behavioral correlates are available. Finally, multiple reviewers suggested that it might be worthwhile to explore a comparison of the arcuate body layer innervation to that of the central bodies of insects, of which there is a richer literature. This is an idea which we were also initially attracted to, and have now added some lines to the discussion section. Our position on this is a cautious one, as a series of more recent comparative studies spanning many insect species using the same antibody, reveals a considerable amount of variation in central body layering even within this clade, which has given us pause in interpreting how substantive similarities and differences to the far more distant spiders would be. Still, this is an interesting avenue which merits an eventual comprehensive analysis, one which would certainly benefit from having additional examples from more spider species, in order to not overstate conclusions based on the currently limited neuroanatomical representation.

Given our framing for the impetus to advance neuroanatomical knowledge in orb-web builders, the question of whether the present findings inform the circuitry controlling web-building is one that naturally follows. While we are unable with this dataset alone to define which brain areas mediate web-building - something which would likely be beyond any anatomical dataset lacking complementary functional data – the process of assembling the atlas has revealed structures and defined innervation patterns in previously ambiguous sectors of the spider brain, particularly in the protocerebrum. A simplistic proposal is that such regions, which are more conspicuous by our techniques and in this model species, would be good candidates for further inquiries into web-building circuitry, as their absence or oversight in past work could be attributable to the different behavioral styles of those model species. Regardless, granted that such a hypothesis cannot be readily refuted by the existing neuroanatomical literature, underscores the need to have more finely refined models of the spider brain, to which we hope that we have positively contributed to and are gratified by the reviewer’s enthusiasm for the strengths of this study.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Brenneis 2022 has done a very nice and comprehensive study focused on the visual system - this might be worth including.

Thank you, we have included this reference on Line 34.

(2) L 29: When talking about "connectivity maps", the emerging connectomes based on EM data could be mentioned.

Additional references have been added, thank you. Line 35.

(3) L 99: Please mention that you are going to describe the brain from ventral to dorsal.

Thank you, we have added a comment to Line 99.

(4) L 13: is found at the posterior.

Thank you, revised.

(5) L 168: How did you pick those two proctolin+ somata, given that there is a lot of additional punctate signal?

Although not visible in this image, if you scroll through the stack there is a neurite which extends from these neurons directly to this area of pronounced immunoreactivity.

(6) Figure 1: Please add the names of the neuropils you go through afterwards.

We have added labels for neuropils which are recognizable externally.

(7) Figure 1 and Figure 5: Please mark the esophagus.

Label has now been added to Figure 1. In Figure 5, the esophagus should not really be visible because these planes are just ventral to its closure.

(8) Figure 5A: I did not see any CCAP signal where the arrow points to; same for 5B (ChAT).

In hindsight, the CCAP point is probably too minor to be worth mentioning, so we have removed it.

The ChAT signal pattern in 5B has been reinforced by adding a dashed circle to show its location as well.

(9) L 249: Could the circular spot also be a tract (many tracts lack synapsin - at least in insects)?

Yes, thank you for pointing this out – the sentence is revised (L274). We are currently further analyzing anti-tubulin volumes and it seem that indeed there are tracts which occupy these synapsin-negative spaces, although interestingly they do not tend to account for the entire space.

(10) L 302: Help me see the "conspicuous" thing.

Brace added to Fig. 8B, note in caption.

(11) L 315: Please first introduce the number of the eyes and how these relate to 1{degree sign} and 2{degree sign} pathway. Are these separate pathways from separate eyes or two relay stations of one visual pathway?

We have expanded the introduction to this section (L336). Yes, these are considered as two separate visual pathways, with a typical segregation of which eyes contribute to which pathway – although there is evidence for species-specific differences in these contributions. In the context of this atlas, we are not currently able to follow which eyes are innervating which pathway.

(12) L 343: It seems that the tonsillar neuropil could be midline spanning (at least this is how I interpret the signal across the midline). Would it make sense to re-formulate from a paired structure to midline-spanning? Would that make it another option for being a central complex homolog?

In the spectrum from totally midline spanning and unpaired (e.g., arcuate body (at least in adults)) to almost fully distinct and paired (e.g., mushroom bodies (although even here there is a midline spanning ‘bridge’)), we view the tonsillar to be more paired due to the oval components, although it does have a midline spanning section, particularly unambiguous just posterior to the oval sections.

Regarding central complex homology, if the suggestion is that the tonsillar with its midline spanning component could represent the entire central complex, then this is a possibility, but it would neglect the highly innervated and layered arcuate body, which we think represent a stronger contender – at least as a component of the central complex. For this reason, we would still be partial to the possibility that the tonsillar is a part of the central complex, but not the entire complex.

(13) L 407: ...and dorsal (..) lobe...

Added the word ‘lobe’ to this sentence (L429).

(14) L 620ff: Maybe mention the role of MBs in learning and memory.

A reference has been added at L661.

(15) L 644: In the context of arcuate body homology with the central body, I was missing a discussion of the neurotransmitters expressed in the respective parts in insects. Would that provide additional arguments?

This is an interesting comparison to explore, and is one that we initially considered making as well. There are certainly commonalities that one could point to, particularly in trying to build the case of whether particular lobes of the arcuate body are similar to the fan-shaped or ellipsoid bodies in insects. Nevertheless, something which has given us pause is studying the more recent comparative works between insect species (Timm et al., 2021, J Comp Neuro, Homberg et al., 2023, J Comp Neuro), which also reveal a fair degree of heterogeneity in expression patterns between species – and this is despite the fact that the neuropils are unambiguously homologous. When comparing to a much more evolutionarily distant organism such as the spider, it becomes less clear which extant species should serve as the best point of comparison, and therefore we fear making specious arguments by focusing on similarities when there are also many differences. We have added some of these comments to the discussion (L699-725).

Throughout the text, I frequently had difficulties in finding the panels right away in the structures mentioned in the text. It would help to number the panels (e.g., 6Ai, Aii, Aii,i etc) and refer to those in the text. Further, all structures mentioned in the text should be labelled with arrows/arrowheads unless they are unequivocally identified in the panel

Thank you for the suggestion. We have adopted the additional numbering scheme for panels, and added additional markers where suggested.

Reviewer #2 (Recommendations for the authors):

(1) L 18: "neurotransmitter" should be pluralized.

Thank you, revised (L18).

(2) L 55: Missing the word "the" before "U. diversus".

Thank you, revised (L57).

(3) L 179: Change synaptic dense to "synapse-dense".

Thank you, revised (L189).

(4) L 570: "present in" would be clearer than "presented on in".

Our intention here was to say that Loesel et al did not show slices from the subesophageal mass for CCAP, so it was ambiguous as to whether it had immunoreactivity there but they simply did not present it, or if it indeed doesn’t show signal in the subesophageal. But agreed, this is awkward phrasing which has been revised (L606-608), thank you.

(5) L 641: It would be worth noting that the upper and lower central bodies are referred to as the fan-shaped and ellipsoid bodies in many insects.

Thank you, this has been added in L694.

(6) L 642: Although cited here regarding insect central body layers, Strausfeld et al. 2006 mainly describe the onychophoran brain and the evolutionary relationship between the onychophoran and chelicerate arcuate bodies. The phylogenetic relationships described here would strengthen the discussion in the section titled "A spider central complex?"

The phylogenetic relationship of onychophorans and chelicerates remains controversial and therefore we find it tricky to use this point to advance the argument in that discussion section, as one could make opposing arguments. The homology of the arcuate body (between chelicerates, onychophorans, and mandibulates) has likewise been argued over, with this Strausfeld et al paper offering one perspective, while others are more permissive (good summary at end of Doeffinger et al., 2010). Our thought was simply to draw attention to grossly similar protocerebral neuropils in examples from distantly related arthropods, without taking a stance, as our data doesn’t really deeply advance one view over the other.

(7) L 701- Noduli have been described in stomatopods (Thoen et al., Front. Behav. Neurosci., 2017).

This is an important addition, thank you – it has been incorporated and cited (L766).

(8) Antisera against DC0 (PKA-C alpha) may distinguish globuli cells from other soma surrounding the mushroom bodies, but this may be accomplished in future studies.

Agreed, this is something we have been interested in, but have not yet acquired the antibody.

Reviewer #3 (Recommendations for the authors):

Overall, this paper is both timely and important. However, it may face some resistance from classically trained arthropod neuroanatomists due to the authors' reliance on immunohistochemistry alone. A method to visualize fiber tracts and neuropil morphology would have been a valuable and grounding complement to the dataset and can be added in future publications. Tract-tracing methods (e.g., dextran injections) would strengthen certain claims about connectivity - particularly those concerning the mushroom bodies. For delineating putative cell populations across regions, fluorescence in situ hybridization for key transcripts would offer convincing evidence, especially in the context of the arcuate body, the tonsillar neuropil, and proposed homologies to the insect central complex.

That said, the dataset remains rich and valuable. Outlined below are a number of issues the authors may wish to address. Most are relatively minor, but a few require further clarification.

(1) Abstract

(a) L 12-14: The authors should frame their work as a novel contribution to our understanding of the spider brain, rather than solely as a tool or stepping stone for future studies. The opening sentences currently undersell the significance of the study.

Thank you for your encourament! We have revised the abstract.

(b) Rather than touting "first of its kind" in the abstract, state what was learned from this.

Thank you, we have revised the abstract.

(c) The abstract does not mention the major results of the study. It should state which brain regions were found. It should list all of the peptides and transmitters that were tested so that they can be discoverable in searches.

Thank you, revised.

(2) Introduction

(a) L 38: There's a more updated reference for Long (2016): Long, S. M. (2021). Variations on a theme: Morphological variation in the secondary eye visual pathway across the order of Araneae. Journal of Comparative Neurology, 529(2), 259-280.

Thank you, this has been updated (L41 and elsewhere).

(b) L 47: While whole-mount imaging offers some benefits, a downside is the need for complete brain dissection from the cuticle, which in spiders likely damages superficial structures (such as the secondary eye pathways).

True – we have added this caveat to the section (L48-51).

(c) L 49-52: If making this claim, more explicit comparisons with non-web building C. saeli in terms of neuropil presence, volume, or density later in the paper would be useful.

We do not have the data on hand to make measured comparisons of C. salei structures, and the neuropils identified in this study are not clearly identifiable in the slices provided in the literature, so would likely require new sample preparations. We’ve removed the reference to proportionality and softened this sentence slightly – we are not trying to make a strong claim, but simply state that this is a possibility.

(3) Results

(a) The authors should state how they accounted for autofluorescence.

While we did not explicitly test for autofluorescence, the long process of establishing a working whole-mount immuno protocol and testing antibodies produced many examples of treated brains which did not show any substantial signal.  We have added a note to the methods section (L866).

(b) L 69: There is some controversy in delineating the subesophageal and supraesophageal mass as the two major divisions despite its ubiquity in the literature. It might be safer to delineate the protocerebrum, deutocerebrum, and fused postoral ganglia (including the pedipalp ganglion) instead.

Thank you for this insight, we have modified the section, section headings and Figure 1 to account for this delineation as well. We have chosen to include both ways of describing the synganglion, in order to maintain a parallel with the past literature, and to be further accessible to non-specialist readers. L73-77

(c) L 90: It might be useful to include a justification for the use of these particular neuropeptides.

Thank you, revised. L97-99.

(d) L 106 - 108: It is stated that the innervation pattern of the leg neuropils is generally consistent, but from Figure 2, it seems that there are differences. The density of 5HT, Proctolin, ChAT, and FMRFamide seems to be higher in the posterior legs. AstA seems to have a broader distribution in L1 and is absent in L4.

We would still stand by the generalization that the innervation pattern is fairly similar for each leg. The L1 neuropils tend to be bigger than the posterior legs, which might explain the difference in density. Another important aspect to keep in mind is that not all of the leg neuropils appear at the exact same imaging plane as we move from ventral to dorsal. If you scroll through the synapsin stack (ventral to dorsal), you will see that L2 and L3 appear first, followed shortly by L1, and then L4, and at the dorsal end of the subesophageal they disappear in the opposite order. The observations listed here are true for the single z-plane in Figure 2, but the fact that they don’t appear at the same time seems to mainly account for these differences. For example, if you scroll further ventrally in the AstA volume, you will see a very similar innervation appear in L4 as well, even though it is absent in the Fig. 2 plane. We plan to have these individual volumes available from a repository so that they can be individually examined to better see the signal at all levels. At the moment, the entire repository can be accessed here: https://doi.org/10.35077/ace-moo-far.

(e) Figure 1 and elsewhere: The axes for the posterior and lateral views show Lateral and Medial. It would be more accurate to label them Left and Right. because it does not define the medial-to-lateral axis. The medial direction is correct for only one hemiganglion, and it's the opposite for the contralateral side.

Thank you, revised.

(f) In Figures that show particular sections, it might be helpful to include a plane in the standard brain to illustrate where that section is.

Yes, we agree and it was our original intention. It is something we can attempt to do, but there is not much room in the corners of many of the synapsin panels, making it harder to make the 3D representation big enough to be clear.

(g) Figure 2, 3: Presenting the z-section stack separately in B and C is awkward because it makes it seem that they are unrelated. I think it would be better to display the z160-190 directly above its corresponding z230-260 for each of the exemplars in B and C. Since there's no left-right asymmetry, a hemibrain could be shown for all examples as was done for TH in D. It's not clear why TH was presented differently.

Thank you for this suggestion. We rearranged the figure as described, but ultimately still found the original layout to be preferrable, in part because the labelling becomes too cramped. We hope that the potential confusion of the continuity of the B and C sections will be mitigated by focusing on the z plane labels and overall shape – which should suggest that the planes are not far from each other. We trust that the form of the leg neuropils is recognizable in both B and C synapsin images, and so readers will make the connection.

Regarding TH, this panel is apart from the rest because we were unable to register the TH volume to the standard brain because the variant of the protocol which produced good anti-TH staining conflicted with synapsin, and we could not simultaneously have adequate penetration of the synapsin signal. We did not want to align the TH panel with the others to avoid potential confusion that this was a view from the same z-plane of a registered volume, as the others are. We have added a note to the figure caption.

(h) The locations of the labels should be consistent. The antisera are below the images in Figure 2, above in Figure 3, and to the bottom left in Figure 5. The slices are shown above in Figure 2 and below in Figure 3.

Thank you, this has been revised for better consistency.

(i) It is surprising to me that there is no mention of the neuronal somata visible in Figure 2 and Figure 3. A typical mapping of the brain would map the locations of the neurons, not just the neuropils.

Our first arrangement of this paper described each immunostain individually from ventral to dorsal, including locations of the immunoreactive somata which could be observed. To aid the flow of the paper and leverage the aligned volumes to emphasize co-expression in the function divisions of the brain, we re-formulated to this current layout which is organized around neuropils. Somata locations are tricky to incorporate in this format of the paper which focuses on key z-planes or tight max projections, because the relevant immunoreactive somata are more dispersed throughout the synganglion, not always overlapping in neighboring z-planes. Further, since only a minority of the antisera we used can reveal traceable projections from the supplying somata in the whole-mount preparation, we would be quite limited in the degree to which we could integrate the specific somata mapping with expression patterns in the neuropil.  Finally, compared to immuno, which can be variable in staining intensity between somata for the same target, we find that FISH reveals these locations more clearly and comprehensively – so while we agree that this mapping would also be useful for the atlas, we would like to better provide this information in a future publication using whole-mount FISH.

(j) L 139: There is a reference to a "brace" in Figure 3B, which does not seem to exist. There's one in Figure 3C.

There is a smaller brace near the bottom of the TDC2 panel in Fig. 3B.

(k) L 151 should be "3D".

Thank you, revised (L160).

(l) Figure 4C: It is not mentioned in the legend that the bottom inset is Proctolin without synapsin.

Thank you, revised (L1213).

(m) L 199: Are the authors sure this subdivision is solely on the anterior-posterior axis? Could it also be dorsal ventral? (i.e., could this be an artifact of the protocerebrum and deutocerebrum?)

Yes, this division can be appreciated to extend somewhat in the dorsal-ventral axis and it is possible that this is the protocerebrum emerging after the deutocerebrum, although this area is largely dorsal to the obvious part of the deutocerebrum. In the horizontal planes there appears to be a boundary line which we use for this subdivision in order to assist in better describing features within this generally ventral part of the protocerebrum – referred to as “stalk” because it is thinner before the protocerebrum expands in size, dorsally. Our intention was more organizational, and as stated in the text, this area is likely heterogenous and we are not suggesting that it has a unified function, so being a visual artifact would not be excluded.

(n) L 249: Could it also indicate large tracts projecting elsewhere?

Yes, definitely, we have evidence that part of the space is occupied by tracts. Revised, thank you (L262).

(o) L 281: Several investigators, including Long (2021,) noted very large and robust mushroom bodies of Nephila.

Thank you – the point is well taken that there are examples of orb-web builders that do have appreciable mushroom bodies. We have added a note in this section (L295), giving the examples of Deinopis spinosa and Argiope trifasciata (Figure 4.20 and 4.22 in Long, 2016).

It looks like these species make the point better than Nephila, as Long lists the mushroom body percentage of total protocerebral volume for D. spinosa as 4.18%, for A. trifasciata as 2.38%, but doesn’t give a percentage for Nephila clavipes (Figure 4.24) and only labels the mushroom bodies structures as “possible” in the figure.

In Long (2021), Nephilidae is described as follows: “In Nephilidae, I found what could be greatly reduced medullae at the caudal end of the laminae, as well as a structure that has many physical hallmarks of reduced mushroom bodies”

(p) L 324: If the authors were able to stain for histamine or supplement this work with a different dissection technique for the dorsal structures, the visual pathways might have been apparent, which seems like a very important set of neuropils to include in a complete brain atlas.

Yes, for this reason histamine has been an interesting target which we have attempted to visualize, but unfortunately have not yet been able to successfully stain for in U. diversus. An additional complication is that the antibodies we have seen call for glutaraldehyde fixation, which may make them incompatible with our approach to producing robust synapsin staining throughout the brain. 

We agree that the lack of the complete visual pathway is a substantial weakness of our preparation, and should be amended in future work, but this will likely require developing a modified approach in order to preserve these delicate structures in U. diversus.

(q) L 331: Is this bulbous shape neuropil, or just the remains of neuropil that were not fully torn away during dissection?

This certainly is a severed part of the primary pathway, although it seems more likely that the bulbous shape is indicative of a neuropil form, rather than just being a happenstance shape that occurred during the breakage. We have examples where the same bulbous shape appears on both sides, and in different brains. It is possible that this may be the principal eye lamina – although we did not see co-staining with expected markers in examples where it did appear, so cannot be sure.

(r) L 354: Is tyraminergic co-staining with the protocerebral bridge enough evidence to speculate that inputs are being supplied?

We agree that this is not compelling, and have removed the statement.

(s) L 372: This whole structure appears to be a previously described structure in spiders, the 'protocerebral commissure'.

We are reasonably sure that what we are calling the PCB is a distinct structure from the protocerebral bridge (PCC). In Babu and Barth’s (1984) horizontal slice (Fig. 11b), you can see the protocerebral commissure immediately adjacent to the mushroom body bridge. It is found similarly located in other species, as can be seen in the supplementary 3D files provided by Steinhoff et al., (2024).

While not visible with synapsin in U. diversus, we likewise can make out a commissure in this area in close proximity to the mushroom body bridge using tubulin staining. What we are calling the protocerebral bridge is a structure which is much more dorsal to the protocerebral commissure, not appearing in the same planes as the MB bridge.

(t) L 377: Do you have an intuition why the tonsillar neuropil and the protocerebral bridge would show limited immunoreactivity, while the arcuate body's is quite extensive?

This is an interesting question. Given the degree of interconnection and the fact that multiple classes of neurons in insects will innervate both central body as well as PCB or noduli, perhaps it would be expected that expression in tonsillar and protocerebral bridge should be commensurate to the innervation by that particular neurotransmitter expressing population in the arcuate body. Apart from the fact that the arcuate body is just bigger, perhaps this points to a great role of the arcuate body for integration, whereas the tonsillar and PCB may engage in more particular processing, or be limited to certain sensory modalities.

Interestingly, it seems that this pattern of more limited immunoreactivity in the PCB and noduli compared with the central bodies (fan-shaped/ellipsoid) also appears in insects (Kahsai et al., 2010, J Comp Neuro, Timm et al., 2021, J Comp Neuro, Homberg et al., 2023, J Comp Neuro) – particularly, with almost every target having at least some layering in the fan-shaped body (Kahsai et al., 2010, J Comp Neuro).  For example, serotoninergic innervation is fairly consistently seen in the upper and lower central bodies across insects, but its presence in the PCB or noduli is more variable – appearing in one or the other in a species-dependent manner (Homberg et al., 2023, J Comp Neuro).

(4) Discussion

(a) L 556: But if confocal images from slices are aligned, is the 3D shape not preserved?

Yes, fair enough – the point we wanted to make was that there is still a limitation in z resolution depending on the thickness of the slices used, which could obscure structures, but perhaps this is too minor of a comment.

(b) L 597: This is a very interesting result. I agree it's likely to do with the processing of mechanosensory information relevant to web activities, and the mushroom body seems like the perfect candidate for this.

(c) L 638: Worth noting that neuropil volume vs density of synapses might play a role in this, as the literature is currently a bit ambiguous with regards to the former.

Thank you, noted (L689).

(d) L 651: The latter seems far more plausible.

Agreed, though the presence of mushroom bodies appears to be variable in spiders, so we didn’t want to take a strong stance, here.

Author response:

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

Public Reviews:

Review #1 (Public review):

Figures 1 through 4 contain data that largely recapitulate published findings (Fulton et al., 2015; Lee et al., 2024; Swee et al., 2016; Dong et al., 2021); it is noted that there is value in confirming phenotypic differences between naive CD5lo and CD5hi CD8 T cells in the NOD background. It is important to contextualize the data while being wary of making parallels with results obtained from CD5lo and CD5hi CD4 T cells. There should also be additional attention paid to the wording in the text describing the data (e.g., the authors assert that, in Figure 4C, the “CD5hi group exhibited higher percentages of CD8+ T cells producing TNF-α, IFN-γ and IL-2” though there is no difference in IL-2 nor consistent differences in TNF-α between the CD5lo and CD5hi population^hi CD8⁺ and CD5^loCD8⁺ T cells have been previously characterized in other genetic backgrounds. In our study, we aimed to confirm and extend these observations specifically in the autoimmune-prone NOD background, which had not been systematically addressed. Additionally, we carefully reviewed the text describing Figure 4C and revised the wording to accurately reflect the observed data (line 263-264). Specifically, we now state that the CD5^hi group exhibited higher levels of IFN-γ and a trend toward increased TNF-α, while IL-2 production did not show a significant difference.

The comparison of CD5 across thymocyte populations is cautioned due to variation in developmental stages, particularly in transgenic models. The reported differences may reflect maturation stages rather than self-reactivity.

We appreciate the reviewer’s important point regarding the interpretation of CD5 levels across thymocyte subsets. In our revised manuscript (lines 455–471), we have added clarification that CD5 expression in DN and DP subsets reflects pre-TCR and TCR signaling events during thymic development. We also acknowledge that differences in maturation stages, especially in the NOD8.3 transgenic model, may influence CD5 expression. We now discuss this caveat and interpret our results with caution, particularly emphasizing that our data support but do not sufficiently define their differential self-reactivity.

The conclusion that PTPN22 overexpression does not inhibit the diabetogenic potential of CD5^hiCD8⁺ T cells is potentially confounded by differences between polyclonal and TCR transgenic systems.

We thank the reviewer for raising this concern. We acknowledge that this system introduces confounders due to differences in precursor frequencies and clonal expansion compared to polyclonal repertoires. These differences may affect the responsiveness to phosphatase-mediated attenuation of signaling. Therefore, while our results support that high-affinity autoreactive CD8⁺ T cells may be less sensitive to PTPN22 overexpression, we do not claim that this finding generalizes to all autoreactive CD8⁺ T cells. Rather, it highlights a potential inability of peripheral tolerance in T cells with strong intrinsic self-reactivity.

TCR sequencing data shows variability; is this representative of the overall repertoire?

We appreciate the reviewer’s comment. We acknowledge that data from bulk TCR sequencing has potential limitations, including variability across experiments and limited resolution at the clonotype level. To improve representativeness and reduce sampling bias, we performed TCR repertoire analysis in two independent experiments. In each experiment, naïve CD5^hi CD8⁺ and CD5^loCD8⁺ T cells were sorted from pooled peripheral lymph nodes of at least 20 individual NOD mice per group. This approach allowed us to capture a broader range of clonotypes and ensured that the resulting repertoire profiles reflect the characteristics of the overall CD5^hi and CD5^lo populations, rather than isolated outliers. Despite some variability, we observed consistent trends in key features, such as shorter CDR3β length, altered TRAV/TRBV usage and reduced diversity in the CD5^hi subset across both experiments. To enhance resolution and directly assess clonotype-specific reactivity, we plan to perform single-cell RNA and TCR sequencing in future studies, as noted in the revised Discussion (lines 466–471).

Clarifications are requested regarding naive gating, controls, gMFI reporting, and missing methods.

We thank the reviewer for these specific suggestions. We have revised figure legends to better describe gating strategies and included appropriate controls in Figures or Supplementary Figures. Regarding gMFI reporting, we have now shown in the figure legends whether values are reported as gMFI. Additionally, we have added the missing methods for cytokine staining, EdU incorporation, overlapped count matrix construction and TCR repertoire diversity metrics.

Review #2 (Public review):

Summary Comment:

The study is nicely performed, but the definition of naive T cells using only CD44 and CD62L may be oversimplified. CD5hi naive T cells express higher CD44 than CD5lo cells.

We thank the reviewer for the critical evaluation and thoughtful comment. As noted, we defined naïve CD8⁺ T cells using a well-established gating strategy based on CD44^lo and CD62L^hi expression, consistent with previous studies (Immunity. 2010; 32(2):214–26; Nat Immunol. 2015; 16(1):107–17). We acknowledge that CD44 is expressed along a continuum, and indeed, within the naïve gate, CD5^hi CD8⁺ T cells exhibited slightly higher CD44 levels compared to their CD5^lo counterparts. However, both subsets remained well below the CD44 expression observed in conventional effector/memory CD8⁺ T cells, supporting their classification as naïve. To further validate this, we assessed additional markers associated with activation and memory differentiation, including CD69, PD-1, KLRG1 and CD25. These analyses confirmed that the sorted CD5^hi and CD5^lo populations retained a phenotypically naïve profile while exhibiting meaningful differences in baseline activation readiness (Figure 1F).

Review #3 (Public review):

CD5 can be regulated by peripheral signals. Therefore, it cannot be concluded that predisposition to effector/memory differentiation is solely programmed in the thymus.

We thank the reviewer for this important point. We agree that CD5 expression can be dynamically regulated in the periphery by tonic TCR signals and antigen encounter, as also reflected in our own data that cells with high CD5 level display elevated activation potential upon encountering antigen (e.g., Figure 3L). To minimize the confounding effects of pre-existing peripheral activation, we performed an adoptive T cell transfer experiment (Figure 4). In this experiment, naïve CD5^hiCD⁺and CD5^loCD8⁺T cells were sorted from the peripheral lymph nodes of young (6–8-week-old) prediabetic NOD mice and transferred into NOD Rag1^–/– recipients. After 4 weeks, we compared the disease phenotypes and functional profiles of CD8⁺ T cells from these two groups. This approach allowed us to evaluate the stability and differentiation capacity of CD5^hi versus CD5^lo cells in a lymphopenic environment, while excluding the possibility that the observed differences were due to already activated CD8⁺T cells at the time of isolation. We have revised the Discussion (lines 440–450) to acknowledge these experimental limitations and clarify that, while our findings demonstrate functional differences between CD5^hiCD8⁺ and CD5^loCD8⁺T cells, we cannot fully exclude contributions from peripheral influences.

Experiments do not explain why PTPN22 overexpression protects in polyclonal T cells but not in NOD8.3 mice.

We appreciate this critical comment. Our findings support that autoreactive T cells with high-affinity TCRs as in NOD8.3 mice receive strong signaling that even PTPN22 overexpression is insufficient to attenuate their activation and effector function. We acknowledge that further mechanistic studies are needed to fully elucidate the differential effects of PTPN22 in polyclonal versus TCR-transgenic settings.

Evidence that PTPN22 does not regulate TCR signaling in NOD8.3 T cells is weak.

We thank the reviewer for this critical comment. Our data show that NOD8.3 T cells with an intrinsic high CD5-associated self-reactivity are more resistant to transgenic Pep-mediated change in the phosphorylation status of TCR signaling molecules CD3ζ and Erk and CD5 expression (Figure 6, B-D). However, we agree that additional functional assays would strengthen this conclusion.

TCR sequencing does not conclusively link CD5hi cells with autoreactivity; single-cell analysis is needed.

We agree with this critical comment. Bulk TCR sequencing revealed repertoire features associated with autoreactivity, but cannot definitively link specific TCRs to function. We have acknowledged this in the discussion (lines 466–471) and highlighted plans to perform single-cell analysis.

CD5hi cells in the PLNs may reflect antigen exposure rather than basal signaling.

We thank the reviewer for this insightful comment. As also noted in Figure 3L, CD5 expression can be influenced by peripheral tonic TCR signals and recent antigen exposure. To minimize the contribution of peripheral activation, we particularly characterized naïve CD8⁺T cells isolated from the peripheral lymph nodes of young (6–8-week-old) prediabetic NOD mice before the onset of overt autoimmunity. Furthermore, we performed an adoptive transfer experiment (Figure 4) using sorted naïve CD5^hiCD8⁺ and CD5^loCD8⁺T cells from these mice and characterized their disease phenotype after 4 weeks in lymphopenic NOD Rag1^–/– recipients and evaluated the effector function of CD8⁺T cells. This approach allowed us to compare the differentiation potential of these subsets in a controlled setting, independent of their activation status at the time of isolation. We have revised the Discussion (lines 440–450) to emphasize that, while our data support functional differences between CD5^hiCD8⁺ and CD5^loCD8⁺T cells, we cannot fully exclude the role of peripheral cues in shaping CD5 expression.

Provide proper gating controls and representative flow plots.

We thank the reviewer for this comment. We have revised figure legends to better describe gating strategies and included representative flow cytometry plots and appropriate gating controls in Figures or Supplementary Figures.

Recommendations for the authors:

Reviewer #1 (Recommendations For The authors):

(1) The figure presentation is inconsistent and the labels/font are often too small to read easily.

As Reviewer suggested, the figure presentation has been revised for consistency. Labels and fonts have been adjusted for improved readability. Specific figures that were difficult to read have been reformatted with larger fonts and clearer legends.

(2) A careful review of the text to ensure clarity of the content is suggested (e.g., “gratitude” at line 91, “were generally lied” at line 123).

Thanks for Reviewer’s comments. The text has been carefully reviewed for clarity and grammatical accuracy. Corrections have been made, including changing “gratitude” to “magnitude” (line 47) and “were generally lied” to “fell between” (line 79).

Reviewer #2 (Recommendations For The Authors):

(1) The definition of naïve T cells based solely on CD44low and CD62Lhigh staining may be oversimplistic. Indeed, even within this definition, naïve CD5high CD8 T cells express much higher levels of CD44 than CD5low CD8 T cells.

Thanks for Reviewer’s comments. We used a literature-supported gating strategy (Immunity. 2010; 32(2):214–26; Nat Immunol. 2015; 16(1):107–17) to define naïve T cells based on CD44^low and CD62L^high expression. It is important to note that CD44 expression exists along a continuum. While we were initially surprised to observe that CD5^loCD8⁺T cells expressed relatively higher levels of CD44 than CD5^loCD8⁺T cells within the naïve gate, both populations still exhibited significantly lower CD44 expression compared to conventional effector/memory CD8⁺T cells. To further validate the distinction between CD5^hi and CD5 subsets, we also examined additional markers such as CD69, PD1, KLRG1 and CD25, which supported their phenotypic differences within the naïve compartment (Figure 1F).

(2) Figure 1G should show the proportion of IGRP-tetramer+ in the three groups of CD8 T cells. Additionally, it would be useful to assess reactivity against a pool of other islet autoantigens using a similar strategy.

As suggested by the reviewer, the revised manuscript now includes additional data showing the proportion of IGRP-tetramer+ cells (Supplementary Figure 1D), as well as reactivity against another islet autoantigen, insulin-1/insulin-2 (Insulin B15–23) (Supplementary Figure 1E). The description of these results, including the proportions of IGRP-tetramer⁺ and Insulin B15–23⁺ CD8⁺Tcells, has been added to lines 126–129 of the revised manuscript.

(3) The resolution of Figure 2 is suboptimal and at places poorly visible. Figure 2D is stated to show “two significant pathways stand out.” In fact, the data are barely significant, and the authors may want to correct their statement.

The resolution of Figure 2 has been improved. As Reviewer suggested, the text has been revised to state “two potential pathways stand out” (line 187) instead of “two significant pathways stand out”.

(4) Figure 3C-F and 3H, showing fold change over baseline values would be much easier for the reader to grasp the data.

As Reviewer suggested, data in Figures 3C-F and 3H now are shown in fold change over baseline values for clarity. Baseline gMFI is the mean of each group (total CD⁺ , CD5^hiCD8⁺ and CD5^loCD8⁺) at 0 μg/ml anti-CD3, with fold changes calculated for stimulation conditions (0.625-10 μg/ml anti-CD3). The figure legend has been updated accordingly.

(5) Figure 4A, it would be much more valuable to show the diabetes frequency upon transfer of CD25- CD4 T cells alone and upon transfer of CD5high CD8 T cells alone. The word “spontaneous” in the Figure 4A legend seems inappropriate.

Thanks for the Reviewer’s comment. We apologize for not including the data for the CD25 CD4⁺ T cell transfer group in the original manuscript. While this group was part of our initial experimental design, we had considered it a control group and unintentionally omitted it from the figure. The revised manuscript now includes this group in Figure 4A. In addition, the term “spontaneous” has been replaced with “diabetes incidence” in the Figure 4A legend and manuscript (line 248). Regarding the suggestion to assess CD5^hiCD8⁺T cells transfer alone, we appreciate the Reviewer’s point. However, previous studies have shown that CD8⁺ T cells alone are not effective and sufficient to induce diabetes in adoptive transfer models, and that effective β-cell destruction typically requires both CD4⁺ and CD8⁺ T cell subsets. For instance, Christianson et al. (1993) demonstrated that enriched CD8⁺ T cells from NOD mice fail to transfer diabetes on their own, while CD4⁺ T cells—particularly from diabetic donors—can induce disease only under specific conditions and are significantly potentiated by co-transfer of CD8⁺cells. These findings have contributed to the widely available standard of co-transferring both subsets when studying diabetogenic potential in NOD models (Diabetes. 1993;42(1):44–55).

(6) Line 257-258, please remove “indicating superior in vivo proliferation by the CD5hi subset.” Indeed, several other possibilities may explain the phenotype, including survival, migration, etc.

As Reviewer suggested, the phrase “indicating superior in vivo proliferation by the CD5^hi subset” has been replaced with “implying increased expansion and activation/effector potential” (line 261).

(7) Figure 5A, it is unclear to this referee what is the significance of CD5 and pCD3zeta expression on DN thymocytes. Do these cells express rearranged alpha/beta TCR? Is it signaling through pre-TCRalpha/TCRbeta pairs?

Thanks a lot for this important question. In the revised manuscript, we have expanded the discussion (line 455–471) to address the developmental significance of CD5 and pCD3ζ expression on DN thymocytes. CD5 expression at this stage reflects pre-TCR signaling strength during early selection, which occurs following successful TCRβ rearrangement. The associated phosphorylation of CD3ζ indicates activation of downstream signaling through the pre-TCRα/TCRβ complex. As discussed in the revised text, these early signals play a critical role in determining lineage progression and self-reactivity tuning. We now acknowledge that signaling at the DN stage occurs through the pre-TCRα/TCRβ heterodimer, not a fully rearranged αβ TCR, and that CD5 expression serves as a marker of the strength of these initial pre-selection signals (Sci Signal. 2022;15(736):eabj9842.). These developmental checkpoints are essential for calibrating TCR sensitivity and ensuring proper thymocyte maturation. This has been clarified in the revised discussion (line 455–471).

(8) Figure 5F, could the DP TCRbeta- CD69- thymocytes from 8.3-TCR NOD mice already express low levels of the self-reactive TCR at this stage to explain their high expression of CD5? Addressing the question experimentally would be useful.

Thanks a lot for this useful comment. According to a review by Huseby et al. (2022), expression of a functional TCRβ chain begins at the DN3 stage, initiating progression through the β-selection checkpoint. This is followed by TRAV locus recombination, resulting in the generation of αβ TCR-expressing double-positive 1 (DP-1) thymocytes. At the DP-1 stage, the quality of TCR signaling driven by self-pMHC interactions governs both positive and negative selection, as well as the development of nonconventional T cell lineages. We hypothesize that in transgenic NOD8.3 mice, which express pre-rearranged Tcra and Tcrb transgenes derived from the islet-reactive CD8⁺T cell clone NY8.3, thymocytes undergo allelic exclusion and lack the clonal diversity seen in non-transgenic mice. As a result, NOD8.3 thymocytes may receive strong TCR signals from early developmental stages (DN3 and DP-1) even without undergoing normal selection checkpoints. While the elevated TCR signal observed in NOD8.3 is indeed artificial, this model provides a unique system to test our hypothesis—namely, whether a strongly self-reactive TCR can generate high basal signaling during thymic development that overrides the negative regulatory effects of phosphatases like Pep. This possibility has been acknowledged in the revised Discussion section, along with a plan to validate the hypothesis experimentally (line 455–471).

(9) Figure 7, single-cell TCR-seq would be much more appropriate to tackle the question of self-reactivity of CD5hi vs. CD5low CD8 T cells.

Thanks a lot for this useful comment. The limitations of bulk TCR-seq are acknowledged, and single-cell TCR-seq is proposed as a future direction (line 455–471).

Note, for Reviewer #2 (Recommendations For The Authors) (7) (8) (9), the discussion paragraphs are included to address the reviewers’ questions (line 455–471).

Reviewer #3 (Recommendations For The Authors):

(1) Positive controls (activated T cells from PLN or spleen), gating controls (whole naïve T cells), and representative flow-cytometry plots are needed for T-bet, EOMES, GzmB, and cytokine staining in Figure 1.

As Reviewer suggested, we added representative gating controls for T-bet, EOMES, GzmB and cytokine staining in Supplementary Figure 1 of revised manuscript.

(2) For Figure 1F, MFI for activation markers for the CD44hiCD62Llo cells should be provided for the comparison of PLN data.

As Reviewer suggested, MFI data for these markers have been included in Figure 1F of revised manuscript.

(3) In many places and figure legends, it is not mentioned from which organ cells were collected, i.e., spleen or PLN.

As Reviewer suggested, the origin of cells for each experiment has been explicitly indicated in the figure legends or figure content to ensure clarity.

(4) In the pancreatic lymph node, autoreactive T cells might be upregulating CD5 because they are encountering antigens. This should be addressed in the discussion.

As Reviewer suggested, this issue has been included in the discussion of revised manuscript (line 440-450).

(5) It is not clear if T cells from the spleen and PLN were stimulated to detect the production of pro-inflammatory cytokines.

Thanks for the critical comment. The stimulation protocol and cytokine staining method have been added to the Supplementary material’s Supplementary methods section Cytokine staining in revised manuscript.

(6) Figure 4C-D: It is not clear if analysis was done on naïve T cells or if they were stimulated.

Thanks for the comment. Additionally, the stimulation and cytokine staining methods used in Figure 4C-D have been described in detail in the Supplementary Materials section Cytokine staining of revised manuscript.

(7) IGRP gating in Figure 4F should be revisited with negative controls.

Thanks for the critical comment. Negative controls have been added and used to adjust IGRP gating, and this is now mentioned in the figure legend of revised manuscript.

(8) Interpretation that only CD5hi cells form a central memory T cell population (Figure 4F) could be misleading.

Thanks for this valuable comment. We agree with that in conventional CD8⁺ T cell immune responses, both CD5^hi and CD5^lo subsets have the potential to differentiate into central memory T cells. In our experimental approach, we adoptively transferred sorted CD5^hiCD8⁺ or CD5^loCD8⁺cells into Rag1^-/- recipients and specifically analyzed PLNs four weeks after transfer. Using CD44 and CD62L expression as conventional markers for central memory T cells, we barely observed a CD44^hiCD62L^hi population in CD5^loCD8⁺transferred group. Based on these results, we stated: “This analysis underscores that the central memory T cell population and the frequency of islet autoantigen-specific CD8⁺T cells are higher in the CD5^hi transferred subset within the PLNs, implying more robust immune responses initiated by the CD5^hicells” (line 272–274). Importantly, we did not intend to imply that only CD5^hi cells can form central memory T cells, but rather that they were more enriched for this phenotype under the specific conditions and time point analyzed. 

(9) IL-2 gating representative plot should be provided for Figure 5A.

As Reviewer suggested, a representative IL-2 gating plot has been included in the revised Supplementary Figure 3B.

Author response:

(1) General Statements

The goal of our study was to mechanistically connect microbiota to host longevity. We have done so using a combination of genetic and physiological experiments, which outline a role for a neuroendocrine relay mediated by the intestinal neuropeptide Tachykinin, and its receptor TkR99D in neurons. We also show a requirement for these genes in metabolic and healthspan effects of microbiota.

The referees' comments suggest they find the data novel and technically sound. We have added data in response to numerous points, which we feel enhance the manuscript further, and we have clarified text as requested. Reviewer #3 identified an error in Figure 4, which we have rectified. We felt that some specific experiments suggested in review would not add significant further depth, as we articulate below.

Altogether our reviewers appear to agree that our manuscript makes a significant contribution to both the microbiome and ageing fields, using a large number of experiments to mechanistically outline the role(s) of various pathways and tissues. We thank the reviewers for their positive contributions to the publication process.

(2) Description of the planned revisions

Reviewer #2:

Not…essential for publication…is it possible to look at Tk protein levels?

We have acquired a small amount of anti-TK antibody and we will attempt to immunostain guts associated with A. pomorum and L. brevis. We are also attempting the equivalent experiment in mouse colon reared with/without a defined microbiota. These experiments are ongoing, but we note that the referee feels that the manuscript is a publishable unit whether these stainings succeed or not.

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

Reviewer #1:

Can the authors state in the figure legends the numbers of flies used for each lifespan and whether replicates have been done?

We have incorporated the requested information into legends for lifespan experiments.

Do the interventions shorten lifespan relative to the axenic cohort? Or do they prevent lifespan extension by axenic conditions? Both statements are valid, and the authors need to be consistent in which one they use to avoid confusing the reader.

We read these statements differently. The only experiment in which a genetic intervention prevented lifespan extension by axenic conditions is neuronal TkR86C knockdown (Figure 6B-C). Otherwise, microbiota shortened lifespan relative to axenic conditions, and genetic knockdowns extend blocked this effect (e.g. see lines 131-133). We have ensured that the framing is consistent throughout, with text edited at lines 198-199, 298-299, 311-312, 345-347, 407-408, 424-425, 450, 497-503.

TkRNAi consistently reduces lipid levels in axenic flies (Figs 2E, 3D), essentially phenocopying the loss of lipid stores seen in control conventionally reared (CR) flies relative to control axenic. This suggests that the previously reported role of Tk in lipid storage - demonstrated through increased lipid levels in TkRNAi flies (Song et al (2014) Cell Rep 9(1): 40) - is dependent on the microbiota. In the absence of the microbiota TkRNAi reduces lipid levels. The lack of acknowledgement of this in the text is confusing

We have added text at lines 219-222 to address this point. We agree that this effect is hard to interpret biologically, since expressing RNAi in axenics has no additional effect on Tk expression (Figure S7). Consequently we can only interpret this unexpected effect as a possible off-target effect of RU feeding on TAG, specific to axenic flies. However, this possibility does not void our conclusion, because an off-target dimunition of TAG cannot explain why CR flies accumulate TAG following Tk^RNAi induction. We hope that our added text clarifies.

I have struggled to follow the authors logic in ablating the IPCs and feel a clear statement on what they expected the outcome to be would help the reader.

We have added the requested statement at lines 423-424, explaining that we expected the IPC ablation to render flies constitutively long-lived and non-responsive to A pomorum.

Can the authors clarify their logic in concluding a role for insulin signalling, and qualify this conclusion with appropriate consideration of alternative hypotheses?

We have added our logic at lines 449-454. In brief, we conclude involvement for insulin signalling because FoxO mutant lifespan does not respond to Tk^RNAi, and diminishes the lifespan-shortening effect of A. pomorum. However, we cannot state that the effects are direct because we do not have data that mechanistically connects Tk/TkR99D signalling directly in insulin-producing cells. The current evidence is most consistent with insulin signalling priming responses to microbiota/Tk/TkR99D, as per the newly-added text.

Typographical errors

We have remedied the highlighted errors, at lines 128-140.

Reviewer #2:

it would be good to show that the bacterial levels are not impacted [by TkRNAi]

We have quantified CFUs in CR flies upon ubiquitous TkRNAi (Figure S5), finding that the RNAi does not affect bacterial load. New text at lines 138-139 articulates this point.

The effect of Tk RNAi on TAG is opposite in CR and Ax or CR and Ap flies, and the knockdown shows an effect in either case (Figure 2E, Figure 3D). Why is this?

As per response to Reviewer #1, we have added text at lines 219-222 to address this point.

Is it possible to perform at least one lifespan repeat with the other Tk RNAi line mentioned?

We have added another experiment showing longevity upon knockdown in conventional flies, using an independent TkRNAi line (Figure S3).

Reviewer #3:

In Line243, the manuscript states that the reporter activity was not increased in the posterior midgut. However, based on the presented results in Fig4E, there is seemingly not apparent regional specificity. A more detailed explanation is necessary.

We thank the reviewer sincerely for their keen eye, which has highlighted an error in the previous version of the figure. In revisiting this figure we have noticed, to our dismay, that the figures for GFP quantification were actually re-plots of the figures for (ac)K quantification. This error led to the discrepancy between statistics and graphics, which thankfully the reviewer noticed. We have revised the figure to remedy our error, and the statistics now match the boxplots and results text.

Fig1C uses Adh for normalization. Given the high variability of the result, the authors should (1) check whether Adh expression levels changed via bacterial association

We selected Adh on the basis of our RNAseq analysis, which showed it was not different between AX and CV guts, whereas many commonly-used “housekeeping” genes were. We have now added a plot to demonstrate (Figure S2).

The statement in Line 82 that EEs express 14 peptide hormones should be supported with an appropriate reference

We have added the requested reference (Hung et al, 2020) at line 86.

(4) Description of analyses that authors prefer not to carry out

Reviewer #1:

I'd encourage the authors to provide lifespan plots that enable comparison between all conditions

We have avoided this approach because the number of survival curves that would need to be presented on the same axis (e.g. 16 for Figure 5) is not legible. However we have ensured that axes on faceted plots are equivalent and with grid lines for comparison. Moreover, our approach using statistical coefficients (EMMs) enables direct quantitative comparison of the differences among conditions.

Reviewer #2:

Is it possible that this driver is simply not resulting in an efficient KD of the receptor? I would be inclined to check this

This comment relates to Figure 7G. We do see an effect of the knockdown in this experiment, so we believe that the knockdown is effective. However the direction of response is not consistent with our hypothesis so the experiment is not informative about the role of these cells. We therefore feel there is little to be gained by testing efficacy of knockdown, which would also be technically challenging because the cells are a small population in a larger tissue which expresses the same transcripts elsewhere (i.e. necessitating FISH).

Would it be possible to use antibodies for acetylated histones?

The comment relates to Figure 4C-E. The proposed studies would be a significant amount of work because, to our knowledge, the specific histone marks which drive activation in TK+ cells remain unknown. On the other hand, we do not see how this information would enrich the present story, rather such experiments would appear to be the beginning of something new. We therefore agree with Reviewer #1 (in cross-commenting) that this additional work is not justified.

Reviewer #3:

Tk+ EEC activity should be assessed directly, rather than relying solely on transcript levels. Approaches such as CaLexA or GCaMP could be used.

We agree with reviewers 1-2 (in cross-commenting) that this proposal is non-trivial and not justified by the additional insight that would be gained. As described above, we are attempting to immunostain Tk, which if successful will provide a third line of evidence for regulation of Tk+ cells. However we note that we already have the strongest possible evidence for a role of these cells via genetic analysis (Figure 5).

While the difficulty of maintaining lifelong axenic conditions is understandable, it may still be feasible to assess the induction of Tk (ie. Tk transcription or EE activity upregulation) by the microbiome on males.

As the reviewer recognises, maintaining axenic experiments for months on end is not trivial. Given the tendency for males either to simply mirror female responses to lifespan-extending interventions, or to not respond at all, we made the decision in our work to only study females. We have instead emphasised in the manuscript that results are from female flies.

TkR86C, in addition to TkR99D, may be involved in the A. pomorum-lifespan interaction. Consider revising the title to refer more generally to the "tachykinin receptor" rather than only TkR99D.

We disagree with this interpretation: the results do not show that TkR86C-RNAi recapitulates the effect of enteric Tk-RNAi. A potentially interesting interaction is apparent, but the data do not support a causal role for TkR86C. A causal role is supported only for TkR99D, knockdown of which recapitulates the longevity of axenic flies and Tk^RNAi flies_._ Therefore we feel that our current title is therefore justified by the data, and a more generic version would misrepresent our findings.

The difference between "aging" and "lifespan" should also be addressed.

The smurf phenotype is a well-established metric of healthspan. Moreover, lifespan is the leading aggregate measure of ageing. We therefore feel that the use of “ageing” in the title is appropriate.

If feasible, assessing foxo activation would add mechanistic depth. This could be done by monitoring foxo nuclear localization or measuring the expression levels of downstream target genes.

Foxo nuclear localisation has already been shown in axenic flies (Shin et al, 2011). We have added text and citation at lines 401-402.

Author response:

We thank the reviewers for their thoughtful, constructive, and generous evaluations of our manuscript. We are encouraged by their overall assessment of the clarity, novelty, and significance of the work, and we appreciate the opportunity to further strengthen the manuscript.

Both reviewers highlight the central contribution of this study: a developmental, circuitlevel dissection of how heart–brain signaling emerges in a vertebrate. We are pleased that the evidence supporting the staggered assembly of vagal motor, sympathetic, and sensory pathways was found to be compelling, and that the computational and experimental framework was viewed as appropriate and informative.

Below, we briefly outline how we plan to address the main points raised in the reviews.

Heart rate variability and temporal structure

Both reviewers note that heart rate variability (HRV) changes across development and suggest that HRV may provide additional insight into the function of autonomic circuits. We agree that HRV is an important physiological readout and that its developmental changes are consistent with the progressive emergence of autonomic control.

In the revised manuscript, we plan to (i) discuss heart rate variability more explicitly in the context of circuit maturation and (ii) clarify the temporal scales captured by our experiments and modeling framework. In particular, we will emphasize that our analyses focus on relationships between neural activity and heart-rate trajectories at timescales accessible given imaging rate and indicator kinetics, rather than beat-to-beat variability. We will also consider adding a supplementary analysis of the variability that can be reliably measured within these constraints, and, where appropriate, how neural activity predicts that measurable variation.

Scope and interpretation of the computational models

Reviewer #2 raises thoughtful points regarding what the generalized linear models can and cannot disambiguate, particularly when multiple efferent pathways may contribute to heart-rate dynamics. We will revise the text to more clearly distinguish between functional encoding relationships inferred from the models and anatomical connectivity that is directly demonstrated.

Our intent is to frame the kernels identified in the motor and sympathetic pathways as computational motifs that capture distinct dynamical contributions, rather than as exclusive or complete explanations of heart-rate control. We will clarify these limitations explicitly in the Results and Discussion.

Circuit diagram and anatomical interpretation

We appreciate the reviewer’s careful reading of the proposed circuit schematic. In the revised manuscript, we will revise the figure and accompanying text to clearly annotate which connections are directly observed, which are functionally inferred, and which remain hypothetical. We will also expand the Discussion to explicitly address open questions, including unresolved feedback pathways and the potential for additional nodes in the circuit.

We believe these revisions will improve clarity without altering the core conclusions of the study. We thank the reviewers again for their insightful feedback and look forward to submitting a revised version of the manuscript that addresses these points in detail.

Author response:

We thank the editors and reviewers for their generally positive and thoughtful feedback on this work. Below are provisional responses to some of the concerns raised:

Reviewer 1:

At a total scan duration of 2 minutes, the ASL sequence utilized in this cohort is much shorter than that of a typical ASL sequence (closer to 5 minutes as mentioned by the authors). However, this implementation also included multiple (n=5) PLDs. As currently described, it is unclear how any repetitions were acquired at each PLD and whether these were acquired efficiently (i.e., with a Look-Locker readout) or whether individual repetitions within this acquisition were dedicated to a single PLD. If the latter, the number of repetitions per PLD (and consequently signal-to-noise-ratio, SNR) is likely to be very low. Have the authors performed any analyses to determine whether the signal in individual subjects generally lies above the noise threshold? This is particularly relevant for white matter, which is the focus of several findings discussed in the study.

We agree that this was a short acquisition compared to most ASL protocols, necessitated by the strict time-keeping requirements for running such a large study. We apologise if this was not clear in the original manuscript, but due to this time constraint and the use of a segmented readout (which was not Look-Locker) there was only time available for a single average at each PLD. This does mean that the perfusion weighted images at each PLD are relatively noisy, although the image quality with this sequence was still reasonable, as demonstrated in Figure 1, with perfusion weighted images visibly above the noise floor. In addition, as has been demonstrated theoretically and experimentally in recent work (Woods et al., 2023, 2020), even though the SNR of each individual PLD image might be low in multi-PLD acquisitions, this is effectively recovered during the model fitting process, giving it comparable or greater accuracy than a protocol which collects many averages at a single (long) PLD. As also noted by the reviewers, this approach has the further benefit of allowing ATT estimation, which has proven to provide useful and complementary information to CBF. Finally, the fact that many of the findings in this study pass strict statistical thresholds for significance, despite the many multiple comparisons performed, and that the spatial patterns of these relationships are consistent with expectations, even in the white matter (e.g. Figure 6B), give us confidence that the perfusion estimation is robust. However, we will consider adding some additional metrics around SNR or fitting uncertainty in a revised manuscript, as well as clarifying details of the acquisition.

Hematocrit is one of the variables regressed out in order to reduce the effect of potential confounding factors on the image-derived phenotypes. The effect of this, however, may be more complex than accounting for other factors (such as age and sex). The authors acknowledge that hematocrit influences ASL signal through its effect on longitudinal blood relaxation rates. However, it is unclear how the authors handled the fact that the longitudinal relaxation of blood (T1Blood) is explicitly needed in the kinetic model for deriving CBF from the ASL data. In addition, while it may reduce false positives related to the relationships between dietary factors and hematocrit, it could also mask the effects of anemia present in the cohort. The concern, therefore, is two-fold: (1) Were individual hematocrit values used to compute T1Blood values? (2) What effect would the deconfounding process have on this?

We agree this is an important point to clarify. In this work we decided not to use the haematocrit to directly estimate the T1 of blood for each participant a) because this would result in slight differences in the model fitting for each subject, which could introduce bias (e.g. the kinetic model used assumes instantaneous exchange between blood water and tissue, so changing the T1 of blood for each subject could make us more sensitive to inaccuracies in this assumption); and b) because typically the haematocrit measures were quite some time (often years) prior to the imaging session, leading to an imperfect correction. We therefore took the pragmatic approach to simply regress each subject’s average haematocrit reading out of the IDP and voxelwise data to prevent it contributing to apparent correlations caused by indirect effects on blood T1. However, we agree with the reviewer that this certainly would mask the effects of anaemia in this cohort, so for researchers interested in this condition a different approach should be taken. We will update the revised manuscript to try to clarify these points.

The authors leverage an observed inverse association between white matter hyperintensity volume and CBF as evidence that white matter perfusion can be sensitively measured using the imaging protocol utilized in this cohort. The relationship between white matter hyperintensities and perfusion, however, is not yet fully understood, and there is disagreement regarding whether this structural imaging marker necessarily represents impaired perfusion. Therefore, it may not be appropriate to use this finding as support for validation of the methodology.

We appreciate the reviewer’s point that there is still debate about the relationship between white matter hyperintensities and perfusion. We therefore agree that this observed relationship therefore does not validate the methodology in the sense that it is an expected finding, but it does demonstrate that the data quality is sufficient to show significant correlations between white matter hyperintensity volume and perfusion, even in white matter regions, which would not be the case if the signal there were dominated by noise. Similarly, the clear spatial pattern of perfusion changes in the white matter that correlate with DTI measures in the same regions also suggests there is sensitivity to white matter perfusion. However, we will update the wording in the revised manuscript to try to clarify this point.

Reviewer 2:

This study primarily serves to illustrate the efficacy and potential of ASL MRI as an imaging parameter in the UK Biobank study, but some of the preliminary observations will be hypothesis-generating for future analyses in larger sample sizes. However, a weakness of the manuscript is that some of the reported observations are difficult to follow. In particular, the associations between ASL and resting fMRI illustrated in Figure 7 and described in the accompanying Results text are difficult to understand. It could also be clearer whether the spatial maps showing ASL correlates of other image-derived phenotypes in Figure 6B are global correlations or confined to specific regions of interest. Finally, while addressing partial volume effects in gray matter regions by covarying for cortical thickness is a reasonable approach, the Methods section seems to imply that a global mean cortical thickness is used, which could be problematic given that cortical thickness changes may be localized.

We apologise if any of the presented information was unclear and will try to improve this in our revised manuscript. To clarify, the spatial maps associated with other (non-ASL) IDPs were generated by calculating the correlation between the ASL CBF or ATT in every voxel in standard space with the non-ASL IDP of interest, not the values of the other imaging modality in the same voxel. No region-based masking was used for this comparison. This allowed us to examine whether the correlation with this non-ASL IDP was only within the same brain region or if the correlations extended to other regions too.

We also agree that the associations between ASL and resting fMRI are not easy to interpret. We therefore tried to be clear in the manuscript that these were preliminary findings that may be of interest to others, but clearly further study is required to explore this complex relationship further. However, we will try to clarify how the results are presented in the revised manuscript.

In relation to partial volume effects, we did indeed use only a global measure of cortical thickness in the deconfounding and we acknowledged that this could be improved in the discussion: [Partial volume effects were] “mitigated here by the inclusion of cortical thickness in the deconfounding process, although a region-specific correction approach that is aware of the through-slice blurring (Boscolo Galazzo et al., 2014) is desirable in future iterations of the ASL analysis pipeline.” As suggested here, although this is a coarse correction, we did not feel that a more comprehensive partial volume correction approach could be used without properly accounting for the through-slice blurring effects from the 3D-GRASE acquisition (that will vary across different brain regions), which is not currently available, although this is an area we are actively working on for future versions of the image analysis pipeline. We again will try to clarify this point further in the revised manuscript.

References

Woods JG, Achten E, Asllani I, Bolar DS, Dai W, Detre J, Fan AP, Fernández-Seara M, Golay X, Günther M, Guo J, Hernandez-Garcia L, Ho M-L, Juttukonda MR, Lu H, MacIntosh BJ, Madhuranthakam AJ, Mutsaerts HJ, Okell TW, Parkes LM, Pinter N, Pinto J, Qin Q, Smits M, Suzuki Y, Thomas DL, Van Osch MJP, Wang DJ, Warnert EAH, Zaharchuk G, Zelaya F, Zhao M, Chappell MA. 2023. Recommendations for Quantitative Cerebral Perfusion MRI using Multi-Timepoint Arterial Spin Labeling: Acquisition, Quantification, and Clinical Applications (preprint). Open Science Framework. doi:10.31219/osf.io/4tskr

Woods JG, Chappell MA, Okell TW. 2020. Designing and comparing optimized pseudo-continuous Arterial Spin Labeling protocols for measurement of cerebral blood flow. NeuroImage 223:117246. doi:10.1016/j.neuroimage.2020.117246

Author response:

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

Public Reviews: 

Reviewer #2 (Public review): 

Summary: 

This is an interesting study exploring methods for reconstructing visual stimuli from neural activity in the mouse visual cortex. Specifically, it uses a competition dataset (published in the Dynamic Sensorium benchmark study) and a recent winning model architecture (DNEM, dynamic neural encoding model) to recover visual information stored in ensembles of mouse visual cortex. 

Strengths: 

This is a great start for a project addressing visual reconstruction. It is based on physiological data obtained at a single-cell resolution, the stimulus movies were reasonably naturalistic and representative of the real world, the study did not ignore important correlates such as eye position and pupil diameter, and of course, the reconstruction quality exceeded anything achieved by previous studies. There appear to be no major technical flaws in the study, and some potential confounds were addressed upon revision. The study is an enjoyable read. 

Weaknesses: 

The study is technically competent and benchmark-focused, but without significant conceptual or theoretical advances. The inclusion of neuronal data broadens the study's appeal, but the work does not explore potential principles of neural coding, which limits its relevance for neuroscience and may create some disappointment to some neuroscientists. The authors are transparent that their goal was methodological rather than explanatory, but this raises the question of why neuronal data were necessary at all, as more significant reconstruction improvements might be achievable using noise-less artificial video encoders alone (network-to-network decoding approaches have been done well by teams such as Han, Poggio, and Cheung, 2023, ICML). Yet, even within the methodological domain, the study does not articulate clear principles or heuristics that could guide future progress. The finding that more neurons improve reconstruction aligns with well-established results in the literature that show that higher neuronal numbers improve decoding in general (for example, Hung, Kreiman, Poggio, and DiCarlo, 2005) and thus may not constitute a novel insight. 

We thank the reviewer for this second round of comments and hope we were able to address the remaining points below. 

Indeed, using surrogate noiseless data is interesting and useful when developing such methods, or to demonstrate that they work in principle. But in order to evaluate if they really work in practice, we need to use real neuronal data. While we did not try movie reconstruction from layers within artificial neural networks as surrogate data, in Supplementary Figure 3C we provide the performance of our method using simulated/predicted neuronal responses from the dynamic neural encoding model alongside real neuronal responses.

Specific issues: 

(1)The study showed that it could achieve high-quality video reconstructions from mouse visual cortex activity using a neural encoding model (DNEM), recovering 10-second video sequences and approaching a two-fold improvement in pixel-by-pixel correlation over attempts. As a reader, I was left with the question: okay, does this mean that we should all switch to DNEM for our investigations of mouse visual cortex? What makes this encoding model special? It is introduced as "a winning model of the Sensorium 2023 competition which achieved a score of 0.301...single trial correlation between predicted and ground truth neuronal activity," but as someone who does not follow this competition (most eLife readers are not likely to do so, either), I do not know how to gauge my response. Is this impressive? What is the best theoretical score, given noise and other limitations? Is the model inspired by the mouse brain in terms of mechanisms or architecture, or was it optimized to win the competition by overfitting it to the nuances of the data set? Of course, I know that as a reader, I am invited to read the references, but the study would stand better on its own, if it clarified how its findings depended on this model. 

The revision helpfully added context to the Methods about the range of scores achieved by other models, but this information remains absent from the Abstract and other important sections. For instance, the Abstract states, "We achieve a pixel-level correlation of 0.57 between the ground truth movie and the reconstructions from single-trial neural responses," yet this point estimate (presented without confidence intervals or comparisons to controls) lacks meaning for readers who are not told how it compares to prior work or what level of performance would be considered strong. Without such context, the manuscript undercuts potentially meaningful achievements. 

We appreciate that the additional information about the performance of the SOTA DNEM to predict neural responses could be made more visible in the paper and will therefore move it from the methods to the results section instead: 

Line 348 “This model achieved an average single-trial correlation between predicted and ground truth neural activity of 0.291 during the competition, this was later improved to 0.301. The competition benchmark models achieved 0.106, 0.164 and 0.197 single-trial correlation, while the third and second place models achieved 0.243 and 0.265. Across the models, a variety of architectural components were used, including 2D and 3D convolutional layers, recurrent layers, and transformers, to name just a few.” will be moved to the results.

With regard to the lack of context for the performance of our reconstruction in the abstract, we may have overcorrected in the previous revision round and have tried to find a compromise which gives more context to the pixel-level correlation value: 

Abstract: “We achieve a pixel-level correlation of 0.57 (95% CI [0.54, 0.60]) between ground-truth movies and single-trial reconstructions. Previous reconstructions based on awake mouse V1 neuronal responses to static images achieved a pixel-level correlation of 0.238 over a similar retinotopic area.”

(2) Along those lines, the authors conclude that "the number of neurons in the dataset and the use of model ensembling are critical for high-quality reconstructions." If true, these principles should generalize across network architectures. I wondered whether the same dependencies would hold for other network types, as this could reveal more general insights. The authors replied that such extensions are expected (since prior work has shown similar effects for static images) but argued that testing this explicitly would require "substantial additional work," be "impractical," and likely not produce "surprising results." While practical difficulty alone is not a sufficient reason to leave an idea untested, I agree that the idea that "more neurons would help" would be unsurprising. The question then becomes: given that this is a conclusion already in the field, what new principle or understanding has been gained in this study? 

As mentioned in our previous round of revisions, we chose not to pursue the comparison of reconstructions using different model architectures in this manuscript because we did not think it would add significant insights to the paper given the amount of work it would require, and we are glad the reviewer agrees. 

While the fact that more neurons result in better reconstructions is unsurprising, how quickly performance drops off will depend on the robustness of the method, and on the dimensionality of the decoding/reconstruction task (decoding grating orientation likely requires fewer neurons than gray scale image reconstruction, which in turn likely requires fewer neurons than full color movie reconstruction). How dependent input optimization based image/movie reconstruction is on population size has not been shown, so we felt it was useful for readers to know how well movie reconstruction works with our method when recording from smaller numbers of neurons. 

(3) One major claim was that the quality of the reconstructions depended on the number of neurons in the dataset. There were approximately 8000 neurons recorded per mouse. The correlation difference between the reconstruction achieved by 1000 neurons and 8000 neurons was ~0.2. Is that a lot or a little? One might hypothesize that 7000 additional neurons could contribute more information, but perhaps, those neurons were redundant if their receptive fields are too close together or if they had the same orientation or spatiotemporal tuning. How correlated were these neurons in response to a given movie? Why did so many neurons offer such a limited increase in correlation? Originally, this question was meant to prompt deeper analysis of the neural data, but the authors did not engage with it, suggesting a limited understanding of the neuronal aspects of the dataset. 

We apologize that we did not engage with this comment enough in the previous round. We assumed that the question arose because there was a misunderstanding about figure 5: 1000 not 1 neuron is sufficient to reconstruct the movies to a pixel-level correlation of 0.344. Of course, the fact that increasing the number of neurons from 1000 to 8000 only increased the reconstruction performance from 0.344 to 0.569 (65% increase in correlation) is still worth discussing. To illustrate this drop in performance qualitatively, we show 3 example frames from movie reconstructions using 1000-8000 neurons in Author response image 1.

Author response image 1.

3 example frames from reconstructions using different numbers of neurons. 

As the reviewer points out, the diminishing returns of additional neurons to reconstruction performance is at least partly because there is redundancy in how a population of neurons represents visual stimuli. In supplementary figure S2, we inferred the on-off receptive fields of the neurons and show that visual space is oversampled in terms of the receptive field positions in panel C. However, the exact slope/shape of the performance vs population size curve we show in Figure 5 will also depend on the maximum performance of our reconstruction method, which is limited in spatial resolution (Figure 4 & Supplementary Figure S5). It is possible that future reconstruction approaches will require fewer neurons than ours, so we interpret this curve rather as a description of the reconstruction method itself than a feature of the underlying neuronal code. For that reason, we chose caution and refrained from making any claims about neuronal coding principles based on this plot. 

(4) We appreciated the experiments testing the capacity of the reconstruction process, by using synthetic stimuli created under a Gaussian process in a noise-free way. But this originally further raised questions: what is the theoretical capability for reconstruction of this processing pipeline, as a whole? Is 0.563 the best that one could achieve given the noisiness and/or neuron count of the Sensorium project? What if the team applied the pipeline to reconstruct the activity of a given artificial neural network's layer (e.g., some ResNet convolutional layer), using hidden units as proxies for neuronal calcium activity? In the revision, this concern was addressed nicely in the review in Supplementary Figure 3C. Also, one appreciates that as a follow up, the team produced error maps (New Figure 6) that highlight where in the frames the reconstruction are likely to fail. But the maps went unanalyzed further, and I am not sure if there was a systematic trend in the errors. 

We are happy to hear that we were able to answer the reviewers’ question of what the maximum theoretical performance of our reconstruction process is in figure 3C. Regarding systematic trends in the error maps, we also did not observe any clear systematic trends. If anything, we noticed that some moving edges were shifted, but we do not think we can quantify this effect with this particular dataset. 

(5) I was encouraged by Figure 4, which shows how the reconstructions succeeded or failed across different spatial frequencies. The authors note that "the reconstruction process failed at high spatial frequencies," yet it also appears to struggle with low spatial frequencies, as the reconstructed images did not produce smooth surfaces (e.g., see the top rows of Figures 4A and 4B). In regions where one would expect a single continuous gradient, the reconstructions instead display specular, high-frequency noise. This issue is difficult to overlook and might deserve further discussion. 

Thank you for pointing this out, this is indeed true. The reconstructions do have high frequency noise. We mention this briefly in line 102 “Finally, we applied a 3D Gaussian filter with sigma 0.5 pixels to remove the remaining static noise (Figure S3) and applied the evaluation mask.” In revisiting this sentence, we think it is more appropriate to replace “remove” with “reduce”. This noise is more visible in the Gaussian noise stimuli (Figure 4) because we did not apply the 3D Gaussian filter to these reconstructions, in case it interfered with the estimates of the reconstruction resolution limits. 

Given that the Gaussian noise and drifting grating stimuli reconstructions were from predicted activity (“noise-free”), this high-frequency noise is not biological in origin and must therefore come from errors in our reconstruction process. This kind of high-frequency noise has previously been observed in feature visualization (optimizing input to maximize the activity of a specific node within a neural network to visualize what that node encodes; Olah, et al., "Feature Visualization", https://distill.pub/2017/feature-visualization/, 2017). It is caused by a kind of overfitting, whereby a solution to the optimization is found that is not “realistic”. Ways of combating this kind of noise include gradient smoothing, image smoothing, and image transformations during optimization, but these methods can restrict the resolution of the features that are recovered. Since we were more interested in determining the maximum resolution of stimuli that can be reconstructed in Figure 4 and Supplementary Figures 5-6, we chose not to apply these methods.

Reviewer #3 (Public review): 

Summary: 

This paper presents a method for reconstructing input videos shown to a mouse from the simultaneously recorded visual cortex activity (two-photon calcium imaging data). The publicly available experimental dataset is taken from a recent brain-encoding challenge, and the (publicly available) neural network model that serves to reconstruct the videos is the winning model from that challenge (by distinct authors). The present study applies gradient-based input optimization by backpropagating the brain-encoding error through this selected model (a method that has been proposed in the past, with other datasets). The main contribution of the paper is, therefore, the choice of applying this existing method to this specific dataset with this specific neural network model. The quantitative results appear to go beyond previous attempts at video input reconstruction (although measured with distinct datasets). The conclusions have potential practical interest for the field of brain decoding, and theoretical interest for possible future uses in functional brain exploration. 

Strengths: 

The authors use a validated optimization method on a recent large-scale dataset, with a state-of-the-art brain encoding model. The use of an ensemble of 7 distinct model instances (trained on distinct subsets of the dataset, with distinct random initializations) significantly improves the reconstructions. The exploration of the relation between reconstruction quality and number of recorded neurons will be useful to those planning future experiments. 

Weaknesses: 

The main contribution is methodological, and the methodology combines pre-existing components without any new original component. 

We thank the reviewer for their balanced assessment of our manuscript.

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

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

This paper presents a method for reconstructing videos from mouse visual cortex neuronal activity using a state-of-the-art dynamic neural encoding model. The authors achieve high-quality reconstructions of 10-second movies at 30 Hz from two-photon calcium imaging data, reporting a 2-fold increase in pixel-by-pixel correlation compared to previous methods. They identify key factors for successful reconstruction including the number of recorded neurons and model ensembling techniques. 

Strengths: 

(1) A comprehensive technical approach combining state-of-the-art neural encoding models with gradient-based optimization for video reconstruction. 

(2) Thorough evaluation of reconstruction quality across different spatial and temporal frequencies using both natural videos and synthetic stimuli. 

(3) Detailed analysis of factors affecting reconstruction quality, including population size and model ensembling effects. 

(4) Clear methodology presentation with well-documented algorithms and reproducible code. 

(5) Potential applications for investigating visual processing phenomena like predictive coding and perceptual learning. 

We thank the reviewer for taking the time to provide this valuable feedback. We would like to add that in our eyes one additional main contribution is the step of going from reconstruction of static images to dynamic videos. We trust that in the revised manuscript, we have now made the point more explicit that static image reconstruction relies on temporally averaged responses, which negates the necessity of having to account for temporal dynamics altogether. 

Weaknesses: 

The main metric of success (pixel correlation) may not be the most meaningful measure of reconstruction quality: 

High correlation may not capture perceptually relevant features.

Different stimuli producing similar neural responses could have low pixel correlations The paper doesn't fully justify why high pixel correlation is a valuable goal 

This is a very relevant point. In retrospect, perhaps we did not justify this enough. Sensory reconstruction typically aims to reconstruct sensory input based on brain activity as faithfully as possible. A brain-to-image decoder might therefore be trained to produce images as close to the original input as possible. The loss function to train the decoder would therefore be image similarity on the pixel level. In that case, evaluating reconstruction performance based on pixel correlation is somewhat circular. 

However, when reconstructing videos, we optimize the input video in terms of its perceptual similarity to the original video and only then evaluate pixel-level similarity. The perceptual similarity metric we optimize for is the estimate of how the neurons in mouse V1 respond to that video. We then evaluate the similarity of this perceptually optimized video to the original input video with pixel-level correlation. In other words, we optimize for perceptual similarity and then evaluate pixel similarity. If our method optimized pixel-level similarity, then we would agree that perceptual similarity is a more relevant evaluation metric. We do not think it was clear in our original submission that our optimization loss function is a perceptual loss function, and have now made this clearer in Figure 1C-D and have clarified this in the results section, line 70:

“In effect, we optimized the input video to be perceptually similar with respect to the recorded neurons.”

And in line 110: 

“Because our optimization of the movies was based on a perceptual loss function, we were interested in how closely these movies matched the originals on the pixel level.”

We chose to use pixel correlation to measure pixel-level similarity for several reasons. 1) It has been used in the past to evaluate reconstruction performance (Yoshida et al., 2020), 2) It is contrast and luminance insensitive, 3) correlation is a common metric so most readers will have an intuitive understanding of how it relates to the data. 

To further highlight why pixel similarity might be interesting to visualize, we have included additional analysis in Figure 6 illustrating pixel-level differences between reconstructions from experimentally recorded activity and predicted activity. 

We expect that the type of perceptual similarity the reviewer is alluding to is pretrained neural network image embedding similarity (Zhang et al., 2018: https://doi.org/10.48550/arXiv.1801.03924). While these metrics seem to match human perceptual similarity, it is unclear if they reflect mouse vision. We did try to compare the embedding similarity from pretrained networks such as VGG16, but got results suggesting the reconstructed frames were no more similar to the ground truth than random frames, which is obviously not true. This might be because the ground truth videos were too different in resolution from the training data of these networks and because these metrics are typically very sensitive to decreases in resolution. 

The best alternative approach to evaluate mouse perceptual similarity would be to show the reconstructed videos to the same animals while recording the same neurons and to compare these neural activation patterns to those evoked by the original ground truth videos. This has been done for static images in the past: Cobos et al., bioRxiv 2022, found that static image reconstructions generated using gradient descent evoked more similar trial-averaged (40 trials) responses to those evoked by ground truth images compared to other reconstruction methods. Unfortunately, we are currently not able to perform these in vivo experiments, which is why we used publicly available data for the current paper. We plan to use this method in the future. But this method is also not flawless as it assumes that the average response to an image is the best reflection of how that image is represented, which may not be the case for an individual trial.

As far as we are aware, there is currently no method that, given a particular activity pattern in response to an image/video, can produce an image/video that induces a neural activity pattern that is closer to the original neural response than simply showing the same image/video again. Hypothetically, such a stimulus exists because of various visual processing phenomena we mention in our discussion (e.g., predictive coding and selective attention), which suggest that the image that is represented by a population of neurons likely differs from the original sensory input. In other words, what the brain represents is an interpretation of reality not a pure reflection. Experimentally verifying this is difficult, as these variations might be present on a single trial level. The first step towards establishing a method that captures the visual representation of a population of neurons is sensory reconstruction, where the aim is to get as close as possible to the original sensory input. We think pixel-level correlation is a stringent and interpretable metric for this purpose, particularly when optimizing for perceptual similarity rather than image similarity directly.

Comparison to previous work (Yoshida et al.) has methodological concerns: Direct comparison of correlation values across different datasets may be misleading; Large differences in the number of recorded neurons (10x more in the current study); Different stimulus types (dynamic vs static) make comparison difficult; No implementation of previous methods on the current dataset or vice versa. 

Yes, we absolutely agree that direct comparison to previous static image reconstruction methods is problematic. We primarily do so because we think it is standard practice to give related baselines. We agree that direct comparison of the performance of video reconstruction methods to image reconstruction methods is not really possible. It does not make sense to train and apply a dynamic model on a static image data set where neural activity is time-averaged, as the temporal kernels could not be learned. Conversely, for a static model, which expects a single image as input and predicts time averaged responses, it does not make sense to feed it a series of temporally correlated movie frames and to simply concatenate the resulting activity perdition. The static model would need to be substantially augmented to incorporate temporal dynamics, which in turn would make it a new method. This puts us in the awkward position of being expected to compare our video reconstruction performance to previous image reconstruction methods without a fair way of doing so. We have now added these caveats in line 119:

“However, we would like to stress that directly comparing static image reconstruction methods with movie reconstruction approaches is fundamentally problematic, as they rely on different data types both during training and evaluation (temporally averaged vs continuous neural activity, images flashed at fixed intervals vs continuous movies).”

We have also toned down the language, emphasising the comparison to previous image reconstruction performance in the abstract, results, and conclusion. 

Abstract: We removed “We achieve a ~2-fold increase in pixel-by-pixel correlation compared to previous state-of-the-art reconstructions of static images from mouse V1, while also capturing temporal dynamics.” and replaced with “We achieve a pixel-level correction of 0.57 between the ground truth movie and the reconstructions from single-trial neural responses.”

Discussion: we removed “In conclusion, we reconstruct videos presented to mice based on the activity of neurons in the mouse visual cortex, with a ~2-fold improvement in pixel-by-pixel correlation compared to previous static image reconstruction methods.” and replaced with “In conclusion, we reconstruct videos presented to mice based on single-trial activity of neurons in the mouse visual cortex.”

We have also removed the performance table and have instead added supplementary figure 3 with in-depth comparison across different versions of our reconstruction method (variations of masking, ensembling, contrast & luminance matching, and Gaussian blurring). 

Limited exploration of how the reconstruction method could provide insights into neural coding principles beyond demonstrating technical capability. 

The aim of this paper was not to reveal principles of neural coding. Instead, we aimed to achieve the best possible performance of video reconstructions and to quantify the limitations. But to highlight its potential we have added two examples of how sensory reconstruction has been applied in human vision research in line 321: 

“Although fMRI-based reconstruction techniques are starting to be used to investigate visual phenomena in humans (such as illusions [Cheng et al., 2023] and mental imagery [Shen et al., 2019; Koide-Majima et al., 2024; Kalantari et al., 2025]), visual processing phenomena are likely difficult to investigate using existing fMRI-based reconstruction approaches, due to the low spatial and temporal resolution of the data.”

We have also added a demonstration of how this method could be used to investigate which parts of a reconstruction from a single trial response differs from the model's prediction (Figure  6). We do this by calculating pixel-level differences between reconstructions from the recorded neural activity and reconstructions from the expected neural activity (predicted activity by the neural encoding model). Although difficult to interpret, this pixel-by-pixel error map could represent trial-by-trial deviations of the neural code from pure sensory representation. But at this point we cannot know whether these errors are nothing more than errors in the reconstruction process. To derive meaningful interpretations of these maps would require a substantial amount of additional work and in vivo experiments and so is outside the scope of this paper, but we include this additional analysis now to highlight a) why pixel-level similarity might be interesting to quantify and visualize and b) to demonstrate how video reconstruction could be used to provide insights into neural coding, namely as a tool to identify how sensory representations differ from a pure reflection of the visual input.  

The claim that "stimulus reconstruction promises a more generalizable approach" (line 180) is not well supported with concrete examples or evidence. 

What we mean by generalizable is the ability to apply reconstruction to novel stimuli, which is not possible for stimulus classification. We now explain this better in the paragraph in line 211: 

“Stimulus identification, i.e. identifying the most likely stimulus from a constrained set, has been a popular approach for quantifying whether a population of neurons encodes the identity of a particular stimulus [Földiák, 1993, Kay et al., 2008]. This approach has, for instance, been used to decode frame identity within a movie [Deitch et al., 2021, Xia et al., 2021, Schneider et al., 2023, Chen et al.,2024]. Some of these approaches have also been used to reorder the frames of the ground truth movie [Schneider et al., 2023] based on the decoded frame identity. Importantly, stimulus identification methods are distinct from stimulus reconstruction where the aim is to recreate what the sensory content of a neuronal code is in a way that generalizes to new sensory stimuli [Rakhimberdina et al., 2021]. This is inherently a more demanding task because the range of possible solutions is much larger. Although stimulus identification is a valuable tool for understanding the information content of a population code, stimulus reconstruction could provide a more generalizable approach, because it can be applied to novel stimuli.”

All the stimuli we reconstructed were not in the training set of the model, i.e., novel. We have also downed down the claim: we have replaced “promises” with “could provide”. 

The paper would benefit from addressing how the method handles cases where different stimuli produce similar neural responses, particularly for high-speed moving stimuli where phase differences might be lost in calcium imaging temporal resolution. 

Thank you for this suggestion, we think this is a great question. Calcium dynamics are slow and some of the high temporal frequency information could indeed be lost, particularly phase information. In other words, when the stimulus has high temporal frequency information, it is harder to decode spatial information because of the slow calcium dynamics. Ideally, we would look at this effect using the drifting grating stimuli; however, this is problematic because we rely on predicted activity from the SOTA DNEM, and due to the dilation of the first convolution, the periodic grating stimulus causes aliasing. At 15Hz, when the temporal frequency of the stimulus is half the movie frame rate, the model is actually being given two static images, and so the predicted activity is the interleaved activity evoked by two static images. We therefore do not think using the grating stimuli is a good idea. But we have used the Gaussian stimuli as it is not periodic, and is therefore less of a problem. 

We have now also reconstructed phase-inverted Gaussian noise stimuli and plotted the video correlation between the reconstructions from activity evoked by phase-inverted stimuli. On the one hand, we find that even for the fastest changing stimuli, the correlation between the reconstructions from phase inverted stimuli are negative, meaning phase information is not lost at high temporal frequencies. On the other hand, for the highest spatial frequency stimuli, the correlation is negative. So, the predicted neural activity (and therefore the reconstructions) are phase-insensitive when the spatial frequency is higher than the reconstruction resolution limit we identified (spatial length constant of 1 pixel, or 3.38 degrees). Beyond this limit, the DNEM predicts activity in response to phase-inverted stimuli, which, when used for reconstruction, results in movies which are more similar to each other than the stimulus that actually evokes them. 

However, not all information is lost at these high spatial frequencies. If we plot the Shannon entropy in the spatial domain or the motion energy in the temporal domain, we find that even when the reconstructions fail to capture the stimulus at a pixel-specific level (spatial length constant of 1 pixel, or 3.38 degrees), they do capture the general spatial and temporal qualities of the videos. 

We have added these additional analyses to Figure 4 and Supplementary Figure 5.

Reviewer #2 (Public review): 

This is an interesting study exploring methods for reconstructing visual stimuli from neural activity in the mouse visual cortex. Specifically, it uses a competition dataset (published in the Dynamic Sensorium benchmark study) and a recent winning model architecture (DNEM, dynamic neural encoding model) to recover visual information stored in ensembles of the mouse visual cortex. 

This is a great project - the physiological data were measured at a single-cell resolution, the movies were reasonably naturalistic and representative of the real world, the study did not ignore important correlates such as eye position and pupil diameter, and of course, the reconstruction quality exceeded anything achieved by previous studies. Overall, it is great that teams are working towards exploring image reconstruction. Arguably, reconstruction may serve as an endgame method for examining the information content within neuronal ensembles - an alternative to training interminable numbers of supervised classifiers, as has been done in other studies. Put differently, if a reconstruction recovers a lot of visual features (maybe most of them), then it tells us a lot about what the visual brain is trying to do: to keep as much information as possible about the natural world in which its internal motor circuits may act consequently. 

While we enjoyed reading the manuscript, we admit that the overall advance was in the range of those that one finds in a great machine learning conference proceedings paper. More specifically, we found no major technical flaws in the study, only a few potential major confounds (which should be addressable with new analyses), and the manuscript did not make claims that were not supported by its findings, yet the specific conceptual advance and significance seemed modest. Below, we will go through some of the claims, and ask about their potential significance. 

We thank the reviewer for the positive feedback on our paper.

(1) The study showed that it could achieve high-quality video reconstructions from mouse visual cortex activity using a neural encoding model (DNEM), recovering 10-second video sequences and approaching a two-fold improvement in pixel-by-pixel correlation over attempts. As a reader, I am left with the question: okay, does this mean that we should all switch to DNEM for our investigations of the mouse visual cortex? What makes this encoding model special? It is introduced as "a winning model of the Sensorium 2023 competition which achieved a score of 0.301... single-trial correlation between predicted and ground truth neuronal activity," but as someone who does not follow this competition (most eLife readers are not likely to do so, either), I do not know how to gauge my response. Is this impressive? What is the best achievable score, in theory, given data noise? Is the model inspired by the mouse brain in terms of mechanisms or architecture, or was it optimized to win the competition by overfitting it to the nuances of the data set? Of course, I know that as a reader, I am invited to read the references, but the study would stand better on its own if clarified how its findings depended on this model. 

This is a very good point. We do not think that everyone should switch to using this particular DNEM to investigate the mouse visual cortex, but we think DNEMs and stimulus reconstruction in general has a lot of potential. We think static neural encoding models have already been demonstrated to be an extremely valuable tool to investigate visual coding (Walker et al., 2019; Yoshida et al., 2021; Willeke et al., bioRxiv 2023). DNEMs are less common, largely because they are very large and are technically more demanding to train and use. That makes static encoding models more practical for some applications, but they do not have temporal kernels and are therefore only used for static stimuli. They cannot, for instance, encode direction tuning, only orientation tuning. But both static and dynamic encoding models have advantages over stimulus classification methods which we outline in our discussion. Here we provide the first demonstration that previous achievements in static image reconstruction are transferable to movies.

It has been shown in the past for static neural encoding models that choosing a better-performing model produces reconstructed static images that are closer to the original image (Pierzchlewicz et al., 2023). The factors in choosing this particular DNEM were its capacity to predict neural activity (benchmarked against other models), it was open source, and the data it was designed for was also available. 

To give more context to the model used in the paper, we have included the following, line 348:

“This model achieved an average single-trial correlation between predicted and ground truth neural activity of 0.291 during the competition, this was later improved to 0.301. The competition benchmark models achieved 0.106, 0.164 and 0.197 single-trial correlation, while the third and second place models achieved 0.243 and 0.265. Across the models, a variety of architectural components were used, including 2D and 3D convolutional layers, recurrent layers, and transformers, to name just a few.” 

Concerning biologically inspired model design. The winning model contained 3 fully connected layers comprising the “Cortex” just before the final readout of neural activity, but we would consider this level of biological inspiration as minor. We do not think that the exact architecture of the model is particularly important, as the crucial aspect of such neural encoders is their ability to predict neural activity irrespective of how they achieve it. There has been a move towards creating foundation models of the brain (Wang et al., 2025) and the priority so far has been on predictive performance over mechanistic interpretability or similarity to biological structures and processes. 

Finally, we would like to note that we do not know what the maximum theoretical score for single-trial responses might be, and don't think there is a good way of estimating it in this context. 

(2) Along those lines, two major conclusions were that "critical for high-quality reconstructions are the number of neurons in the dataset and the use of model ensembling." If true, then these principles should be applicable to networks with different architectures. How well can they do with other network types? 

This is a good question. Our method critically relies on the accurate prediction of neural activity in response to new videos. It is therefore expected that a model that better predicts neural responses to stimuli will also be better at reconstructing those stimuli given population activity. This was previously shown for static images (Pierzchlewicz et al., 2023). It is also expected that whenever the neural activity is accurately predicted, the corresponding reconstructed frames will also be more similar to the ground truth frames. We have now demonstrated this relationship between prediction accuracy and reconstruction accuracy in supplementary figure 4.

Although it would be interesting to compare the movie reconstruction performance of many different models with different architectures and activity prediction performances, this would involve quite substantial additional work because movie reconstruction is very resource- and time-intensive. Finding optimal hyperparameters to make such a comparison fair and informative would therefore be impractical and likely not yield surprising results. 

We also think it is unlikely that ensembling would not improve reconstruction performance in other models because ensembling across model predictions is a common way of improving single-model performance in machine learning. Likewise, we think it is unlikely that the relationship between neural population size and reconstruction performance would differ substantially when using different models, because using more neurons means that a larger population of noisy neurons is “voting” on what the stimulus is. However, we would expect that if the model were worse at predicting neural activity, then more neurons are needed for an equivalent reconstruction performance. In general, we would recommend choosing the best possible DNEM available, in terms of neural activity prediction performance, when reconstructing movies using input optimization through gradient descent. 

(3) One major claim was that the quality of the reconstructions depended on the number of neurons in the dataset. There were approximately 8000 neurons recorded per mouse. The correlation difference between the reconstruction achieved by 1 neuron and 8000 neurons was ~0.2. Is that a lot or a little? One might hypothesize that ~7,999 additional neurons could contribute more information, but perhaps, those neurons were redundant if their receptive fields were too close together or if they had the same orientation or spatiotemporal tuning. How correlated were these neurons in response to a given movie? Why did so many neurons offer such a limited increase in correlation? 

In the population ablation experiments, we compared the performance using ~1000, ~2000, ~4000, ~8000 neurons, and found an attenuation of 39.5% in video correlation when dropping 87.5% of the neurons (~1000 neurons remaining), we did not try reconstruction using just 1 neuron. 

(4) On a related note, the authors address the confound of RF location and extent. The study resorted to the use of a mask on the image during reconstruction, applied during training and evaluation (Line 87). The mask depends on pixels that contribute to the accurate prediction of neuronal activity. The problem for me is that it reads as if the RF/mask estimate was obtained during the very same process of reconstruction optimization, which could be considered a form of double-dipping (see the "Dead salmon" article, https://doi.org/10.1016/S1053-8119(09)71202-9). This could inflate the reconstruction estimate. My concern would be ameliorated if the mask was obtained using a held-out set of movies or image presentations; further, the mask should shift with eye position, if it indeed corresponded to the "collective receptive field of the neural population." Ideally, the team would also provide the characteristics of these putative RFs, such as their weight and spatial distribution, and whether they matched the biological receptive fields of the neurons (if measured independently). 

We can reassure the reviewer that there is no double-dipping. We would like to clarify that the mask was trained only on videos from the training set of the DNEM and not the videos which were reconstructed. We have added the sentence, line 91: 

“None of the reconstructed movies were used in the optimization of this transparency mask.”

Making the mask dependent on eye position would be difficult to implement with the current DNEM, where eye position is fed to the model as an additional channel. When using a model where the image is first transformed into retinotopic coordinates in an eye position-dependent manner (such as in Wang et al., 2025) the mask could be applied in retinotopic coordinates and therefore be dependent on eye position. 

Effectively, the alpha mask defines the relative level of influence each pixel contributes to neural activity prediction. We agree it is useful to compare the shape of the alpha mask with the location of traditional on-off receptive fields (RFs) to clarify what the alpha mask represents and characterise the neural population available for our reconstructions. We therefore presented the DNEM with on-off patches to map the receptive fields of single neurons in an in silico experiment (the experimentally derived RF are not available). As expected, there is a rough overlap between the alpha mask (Supplementary Figure 2D), the average population receptive field (Supplementary Figure 2B), and the location of receptive field peaks (Supplementary Figure 2C). In principle, all three could be used during training or evaluation for masking, but we think that defining a mask based on the general influence of images on neural activity, rather than just on off patch responses, is a more elegant solution.

One idea of how to go a step further would be to first set the alpha mask threshold during training based on the % loss of neural activity prediction performance that threshold induces (in our case alpha=0.5 corresponds to ~3% loss in correlation between predicted vs recorded neural responses, see Supplementary Figure 3D), and second base the evaluation mask on a pixel correlation threshold (see example pixel correlation map in Supplementary Figure 2E) instead to avoid evaluating areas of the image with low image reconstruction confidence. 

We referred to this figure in the result section, line 83:

“The transparency masks are aligned with but not identical to the On-Off receptive field distribution maps using sparse-noise (Figure S2).” 

We have also done additional analysis on the effect of masking during training and evaluation with different thresholds in Supplementary Figure 3.

(5) We appreciated the experiments testing the capacity of the reconstruction process, by using synthetic stimuli created under a Gaussian process in a noise-free way. But this further raised questions: what is the theoretical capability for the reconstruction of this processing pipeline, as a whole? Is 0.563 the best that one could achieve given the noisiness and/or neuron count of the Sensorium project? What if the team applied the pipeline to reconstruct the activity of a given artificial neural network's layer (e.g., some ResNet convolutional layer), using hidden units as proxies for neuronal calcium activity? 

That’s a very interesting point. It is very hard to know what the theoretical best reconstruction performance of the model would be. Reconstruction performance could be decreased due to neural variability, experimental noise, the temporal kernel of the calcium indicator and the imaging frame rate, information compression along the visual hierarchy, visual processing phenomena (such as predictive coding and selective attention), failure of the model to predict neural activity correctly, or failure of the reconstruction process to find the best possible image which explains the neural activity. We don't think we can disentangle the contribution of all these sources, but we can provide a theoretical maximum assuming that the model and the reconstruction process are optimal. To that end, we performed additional simulations and reconstructed the natural videos using the predicted activity of the neurons in response to the natural videos as the target (similar to the synthetic stimuli) and got a correlation of 0.766. So, the single trial performance of 0.569 is ~75% of this theoretical maximum. This difference can be interpreted as a combination of the losses due to neuronal variability, measurement noise, and actual deviations in the images represented by the brain compared to reality. 

We thank the reviewer for this suggestion, as it gave us the idea of looking at error maps (Figure 6), where the pixel-level deviation of the reconstructions from recorded vs predicted activity is overlaid on the ground truth movie.

(6) As the authors mentioned, this reconstruction method provided a more accurate way to investigate how neurons process visual information. However, this method consisted of two parts: one was the state-of-the-art (SOTA) dynamic neural encoding model (DNEM), which predicts neuronal activity from the input video, and the other part reconstructed the video to produce a response similar to the predicted neuronal activity. Therefore, the reconstructed video was related to neuronal activity through an intermediate model (i.e., SOTA DNEM). If one observes a failure in reconstructing certain visual features of the video (for example, high-spatial frequency details), the reader does not know whether this failure was due to a lack of information in the neural code itself or a failure of the neuronal model to capture this information from the neural code (assuming a perfect reconstruction process). Could the authors address this by outlining the limitations of the SOTA DNEM encoding model and disentangling failures in the reconstruction from failures in the encoding model? 

To test if a better neural prediction by the DNEM would result in better reconstructions, we ran additional simulations and now show that neural activity prediction performance correlates with reconstruction performance (Supplementary Figure 4B). This is consistent with Pierzchlewicz et al., (2023) who showed that static image reconstructions using better encoding models leads to better reconstruction performance. As also mentioned in the answer to the previous comment, untangling the relative contributions of reconstruction losses is hard, but we think that improvements to the DNEM performance are key. Two suggestions to improving the DNEM we used would be to translate the input image into retinotopic coordinates and shift this image relative to eye position before passing it to the first convolutional layer (as is done in Wang et al. 2025), to use movies which are not spatially down sampled as heavily, to not use a dilation of 2 in the temporal convolution of the first layer and to train on a larger dataset. 

(7) The authors mentioned that a key factor in achieving high-quality reconstructions was model assembling. However, this averaging acts as a form of smoothing, which reduces the reconstruction's acuity and may limit the high-frequency content of the videos (as mentioned in the manuscript). This averaging constrains the tool's capacity to assess how visual neurons process the low-frequency content of visual input. Perhaps the authors could elaborate on potential approaches to address this limitation, given the critical importance of high-frequency visual features for our visual perception. 

This is exactly what we also thought. To answer this point more specifically, we ran additional simulations where we also reconstruct the movies using gradient ensembling instead of reconstruction ensembling. Here, the gradients of the loss with respect to each pixel of the movie is calculated for each of the model instances and are averaged at every iteration of the reconstruction optimization. In essence, this means that one reconstruction solution is found, and the averaging across reconstructions, which could degrade high-frequency content, is skipped. The reconstructions from both methods look very similar, and the video correlation is, if anything, slightly worse (Supplemental Figure 3A&C). This indicates that our original ensembling approach did not limit reconstruction performance, but that both approaches can be used, depending on what is more convenient given hardware restrictions. 

Reviewer #3 (Public review): 

Summary: 

This paper presents a method for reconstructing input videos shown to a mouse from the simultaneously recorded visual cortex activity (two-photon calcium imaging data). The publicly available experimental dataset is taken from a recent brain-encoding challenge, and the (publicly available) neural network model that serves to reconstruct the videos is the winning model from that challenge (by distinct authors). The present study applies gradient-based input optimization by backpropagating the brain-encoding error through this selected model (a method that has been proposed in the past, with other datasets). The main contribution of the paper is, therefore, the choice of applying this existing method to this specific dataset with this specific neural network model. The quantitative results appear to go beyond previous attempts at video input reconstruction (although measured with distinct datasets). The conclusions have potential practical interest for the field of brain decoding, and theoretical interest for possible future uses in functional brain exploration. 

Strengths: 

The authors use a validated optimization method on a recent large-scale dataset, with a state-of-the-art brain encoding model. The use of an ensemble of 7 distinct model instances (trained on distinct subsets of the dataset, with distinct random initializations) significantly improves the reconstructions. The exploration of the relation between reconstruction quality and the number of recorded neurons will be useful to those planning future experiments. 

Weaknesses: 

The main contribution is methodological, and the methodology combines pre-existing components without any new original components. 

We thank the reviewer for taking the time to review our paper and for their overall positive assessment. We would like to emphasise that combining pre-existing machine learning techniques to achieve top results in a new modality does require iteration and innovation. While gradient-based input optimization by backpropagating the brain-encoding error through a neural encoding model has been used in 2D static image optimization to generate maximally exciting images and reconstruct static images, we are the first to have applied it to movies which required accounting for the time domain. Previous methods used time averaged responses and were limited to the reconstruction of static images presented with fixed image intervals.

The movie reconstructions include a learned "transparency mask" to concentrate on the most informative area of the frame; it is not clear how this choice impacts the comparison with prior experiments. Did they all employ this same strategy? If not, shouldn't the quantitative results also be reported without masking, for a fair comparison? 

Yes, absolutely. All reconstruction approaches limit the field of view in some way, whether this is due to the size of the screen, the size of the image on the screen, or cropping of the presented/reconstructed images during analysis due to the retinotopic coverage of the recorded neurons. Note that we reconstruct a larger field of view than Yoshida et al. In Yoshida et al., the reconstructed field of view was 43 by 43 retinal degrees. we show the size of an example evaluation mask in comparison. 

To address the reviewer’s concern more specifically, we performed additional simulations and now also show the performance using a variety of different training and evaluation masks, including different alpha thresholds for training and evaluation masks as well as the effective retinotopic coverage at different alpha thresholds. Despite these comparisons, we would also like to highlight that the comparison to the benchmark is problematic itself. This is because image and movie reconstruction are not directly comparable. It does not make sense to train and apply a dynamic model on a static image dataset where neural activity is time averaged. Conversely, it does not make sense to train or apply a static model that expects time-averaged neural responses on continuous neural activity unless it is substantially augmented to incorporate temporal dynamics, which in turn would make it a new method. This puts us in the awkward position of being expected to compare our video reconstruction performance to previous image reconstruction methods without a fair way of doing so. We have therefore de-emphasised the phrasing comparing our method to previous publications in the abstract, results, and discussion. 

Abstract: “We achieve a ~2-fold increase in pixel-by-pixel correlation compared to previous state-of-the-art reconstructions of static images from mouse V1, while also capturing temporal dynamics.” with “We achieve a pixel-level correction of 0.57 between the ground truth movie and the reconstructions from single-trial neural responses.”

Results: “This represents a ~2x higher pixel-level correlation over previous single-trial static image reconstructions from V1 in awake mice (image correlation 0.238 +/- 0.054 s.e.m for awake mice) [Yoshida et al., 2020] over a similar retinotopic area (~43° x 43°) while also capturing temporal dynamics. However, we would like to stress that directly comparing static image reconstruction methods with movie reconstruction approaches is fundamentally problematic, as they rely on different data types both during training and evaluation (temporally averaged vs continuous neural activity, images flashed at fixed intervals vs continuous movies).”

Discussion: “In conclusion, we reconstruct videos presented to mice based on the activity of neurons in the mouse visual cortex, with a ~2-fold improvement in pixel-by-pixel correlation compared to previous static image reconstruction methods.” with “In conclusion, we reconstruct videos presented to mice based on single-trial activity of neurons in the mouse visual cortex.”

We have also removed the performance table and have instead added supplementary figure 3 with in-depth comparison across different versions of our reconstruction method (variations of masking, ensembling, contrast & luminance matching, and Gaussian blurring). 

We believe that we have given enough information in our paper now so that readers can make an informed decision whether our movie reconstruction method is appropriate for the questions they are interested in.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors): 

(1) "Reconstructions have been luminance (mean pixel value across video) and contrast (standard deviation of pixel values across video) matched to ground truth." This was not clear: was it done by the investigating team? I imagine that one of the most easily captured visual features is luminance and contrast, why wouldn't the optimization titrate these well? 

The contrast and luminance matching of the reconstructions to the ground truth videos was done by us, but this was only done to help readers assess the quality of the reconstructions by eye. Our performance metrics (frame and video correlation) are contrast and luminance insensitive. To clarify this, we have also added examples of non-adjusted frames in Supplementary Figure 3A, and added a sentence in the results, line 103: 

“When presenting videos in this paper we normalize the mean and standard deviation of the reconstructions to the average and standard deviation of the corresponding ground truth movie before applying the evaluation masks, but this is not done for quantification except in Supplementary Figure 3D.”

We were also initially surprised that contrast and luminance are not captured well by our reconstruction method, but this makes sense as V1 is largely luminance invariant (O’Shea et al., 2025 https://doi.org/10.1016/j.celrep.2024.115217 ) and contrast only has a gain effect on V1 activity (Tring et al., 2024 https://journals.physiology.org/doi/full/10.1152/jn.00336.2024). Decoding absolute contrast is likely unreliable because it is probably not the only factor modulating the overall gain of the neural population.

To address the reviewer’s comment more fully, we ran additional experiments. More specifically, to test why contrast and luminance are not recovered in the reconstructions, we checked how the predicted activity between the reconstruction and the contrast/luminance corrected reconstructions differs. Contrast and luminance adjustment had little impact on predicted response similarity on average. This makes the reconstruction optimization loss function insensitive to overall contrast and luminance so it cannot be decoded. There is a small effect on activity correlation, however, so we cannot completely rule out that contrast and luminance could be reconstructed with a different loss function. 

(2) The authors attempted to investigate the variability in reconstruction quality across different movies and 10-second snippets of a movie by correlating various visual features, such as video motion energy, contrast, luminance, and behavioral factors like running speed, pupil diameter, and eye movement, with reconstruction success. However, it would also be beneficial if the authors correlated the response loss (Poisson loss between neural responses) with reconstruction quality (video correlation) for individual videos, as these metrics are expected to be correlated if the reconstruction captures neural variance. 

We thank the reviewer for this suggestion. We have now included this analysis and find that if the neural activity was better predicted by the DNEM then the reconstruction of the video was also more similar to the ground truth video. We further found that this effect is shift-dependent (in time), meaning the prediction of activity based on proximal video frames is more influential on reconstruction performance. 

Reviewer #3 (Recommendations for the authors): 

(1) I was confused about the choice of applying a transparency mask thresholded with alpha>0.5 during training and alpha>1 during evaluation. Why treat the two situations differently? Also, shouldn't we expect alpha to be in the [0,1] range, in which case, what is the meaning of alpha>1? (And finally, as already described in "Weaknesses", how does this choice impact the comparison with prior experiments? Did they also employ a similar masking strategy?) 

We found that applying a mask during training increased performance regardless of the size of the evaluation mask. Using a less stringent mask during training than during evaluation increases performance slightly, but also allows inspection of the reconstruction in areas where the model will be less confident without sacrificing performance, if this is desired. The thresholds of 0.5 and 1 were chosen through trial and error, but the exact values do not hold intrinsic meaning. The alpha mask values can go above 1 during their optimization. We could have clipped alpha during the training procedure (algorithm 1), but we decided this was not worth redoing at this stage, as the alphas used for testing were not above 1. All reconstruction approaches in previous publications limit the field of view in some form, whether this is due to the size of the screen, the size of the image on the screen, or the cropping of the presented/reconstructed images during analysis. 

To address the reviewer’s comment in detail, we have added extensive additional analysis to evaluate the coverage of the reconstruction achieved in this paper and how different masking strategies affect performance, as well as how the mask relates to more traditional receptive field mapping.  

(2) I would not use the word "imagery" in the first sentence of the abstract, because this might be interpreted by some readers as reconstruction of mental imagery, a very distinct question. 

We changed imagery to images in the abstract.

(3) Line 145-146: "<1 frame, or <30Hz" should be "<1 frame, or >30Hz". 

We have corrected the error.

(4) Algorithm 1, Line 5, a subscript variable 'g' should be changed to 'h'

We have corrected the error.

Additional Changes

(1) Minor grammatical errors

(2) Addition of citations: We were previously not aware of a bioRxiv preprint from 2022 (Cobos et al., 2022), which used gradient descent-based input optimization to reconstruct static images but without the addition of a diffusion model. Instead, we had cited for this method Pierzchlewicz et al., 2023 bioRxiv/NeurIPS. In Cobos et al., 2022, they compare static image reconstruction similarity to ground truth images and the similarity of the in vivo evoked activity across multiple reconstruction methods. Performance values are only given for reconstructions from trial-averaged responses across ~40 trials (in the absence of original data or code we are also not able to retrospectively calculate single-trial performance). The authors find that optimizing for evoked activity rather than image similarity produces image reconstructions that evoke more similar in vivo responses compared to reconstructions optimized for image similarity itself. We have now added and discussed the citation in the main text. 

(3) Workaround for error in the open-source code from https://github.com/lRomul/sensorium for video hashing function in the SOTA DNEM: By checking the most correlated first frame for each reconstructed movie, we discovered there was a bug in the open-source code and 9/50 movies we originally used for reconstruction were not properly excluded from the training data between DNEM instances. The reason for this error was that some of the movies are different by only a few pixels, and the video hashing function used to split training and test set folds in the original DNEM code classified these movies as different and split them across folds. We have replaced these 9 movies and provide a figure below showing the next closest first frame for every movie clip we reconstruct. This does not affect our claims. Excluding these 9 movie clips, did not affect the reconstruction performance (video correlation went from 0.563 to 0.568), so there was no overestimation of performance due to test set contamination. However, they should still be removed so some of the values in the paper have changed slightly. The only statistical test that was affected was the correlation between video correlation and mean motion energy (Supplementary Figure 4A), which went from p = 0.043 to 0.071. 

Author response image 2.

exclusion of movie clips with duplicates in the DNEM training data. A) example frame of a reconstructed movie (ground truth) and the most correlated first frame from the training data. b) all movie clips and their corresponding most correlated clip from the training data. Red boxes indicate excluded duplicates. 

Author response:

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

Public Reviews:

Reviewer #1 (Public review)

Major:

(1) In line 76, the authors make a very powerful statement: 'σRNN simulation achieves higher similarity with unseen recorded trials before perturbation, but lower than the bioRNN on perturbed trials.' I couldn't find a figure showing this. This might be buried somewhere and, in my opinion, deserves some spotlight - maybe a figure or even inclusion in the abstract.

We agree with the reviewer that these results are important. The failure of σRNN on perturbed data could be inferred from the former Figures 1E, 2C-E, and 3D. Following the reviewers' comments, we have tried to make this the most prominent message of Figure 1, in particular with the addition of the new panel E. We also moved Table 1 from the  Supplementary to the main text to highlight this quantitatively. 

(2) It's mentioned in the introduction (line 84) and elsewhere (e.g., line 259) that spiking has some advantage, but I don't see any figure supporting this claim. In fact, spiking seems not to matter (Figure 2C, E). Please clarify how spiking improves performance, and if it does not, acknowledge that. Relatedly, in line 246, the authors state that 'spiking is a better metric but not significant' when discussing simulations. Either remove this statement and assume spiking is not relevant, or increase the number of simulations.

We could not find the exact quote from the reviewer, and we believe that he intended to quote “spiking is better on all metrics, but without significant margins”. Indeed, spiking did not improve the fit significantly on perturbed trials, this is particularly true in comparison with the benefits of Dale’s law and local inhibition. As suggested by the reviewer, we rephrased the sentence from this quote and more generally the corresponding paragraphs in the intro (lines 83-87) and in the results (lines 245-271). Our corrections in the results sections are also intended to address the minor point (4) raised by the same reviewer.

(3) The authors prefer the metric of predicting hits over MSE, especially when looking at real data (Figure 3). I would bring the supplementary results into the main figures, as both metrics are very nicely complementary. Relatedly, why not add Pearson correlation or R2, and not just focus on MSE Loss?

In Figure 3 for the in-vivo data, we do not have simultaneous electrophysiological recordings and optogenetic stimulation in this dataset.  The two are performed on different recording sessions. Therefore, we can only compare the effect of optogenetics on the behavior, and we cannot compute Pearson correlation or R2 of the perturbed network activity. To avoid ambiguity, we wrote “For the sessions of the in vivo dataset with optogenetic perturbation that we considered, only the behavior of an animal is recorded” on line 294. 

(4) I really like the 'forward-looking' experiment in closed loop! But I felt that the relevance of micro perturbations is very unclear in the intro and results. This could be better motivated: why should an experimentalist care about this forward-looking experiment? Why exactly do we care about micro perturbation (e.g., in contrast to non-micro perturbation)? Relatedly, I would try to explain this in the intro without resorting to technical jargon like 'gradients'.

As suggested, we updated the last paragraph of the introduction (lines 88 - 95) to give better motivation for why algorithmically targeted acute spatio-temporal perturbations can be important to dissect the function of neural circuits. We also added citations to recent studies with targeted in vivo optogenetic stimulation. As far as we know the existing previous work targeted network stimulation mostly using linear models, while we used non-linear RNNs and their gradients.

Minor:

(1) In the intro, the authors refer to 'the field' twice. Personally, I find this term odd. I would opt for something like 'in neuroscience'.

We implemented the suggested change: l.27 and l.30

(2) Line 45: When referring to previous work using data-constrained RNN models, Valente et al. is missing (though it is well cited later when discussing regularization through low-rank constraints)

We added the citation: l.45

(3) Line 11: Method should be methods (missing an 's').

We fixed the typo.

(4) In line 250, starting with 'So far', is a strange choice of presentation order. After interpreting the results for other biological ingredients, the authors introduce a new one. I would first introduce all ingredients and then interpret. It's telling that the authors jump back to 2B after discussing 2C.

We restructured the last two paragraphs of section 2.1, and we hope that the presentation order is now more logical.

(5) The black dots in Figure 3E are not explained, or at least I couldn't find an explanation.

We added an explanation in the caption of Figure 3E.

Reviewer #2 (Public review):

(1) Some aspects of the methods are unclear. For comparisons between recurrent networks trained from randomly initialized weights, I would expect that many initializations were made for each model variant to be compared, and that the performance characteristics are constructed by aggregating over networks trained from multiple random initializations. I could not tell from the methods whether this was done or how many models were aggregated.

The expectation of the reviewer is correct, we trained multiple models with different random seeds (affecting both the weight initialization and the noise of our model) for each variant and aggregated the results. We have now clarified this in Methods 4.6. lines 658-662.

(2) It is possible that including perturbation trials in the training sets would improve model performance across conditions, including held-out (untrained) perturbations (for instance, to units that had not been perturbed during training). It could be noted that if perturbations are available, their use may alleviate some of the design decisions that are evaluated here.

In general, we agree with the reviewer that including perturbation trials in the training set would likely improve model performance across conditions. One practical limitation explaining partially why we did not do it with our dataset is the small quantity of perturbed trials for each targeted cortical area: the number of trials with light perturbations is too scarce to robustly train and test our models.

More profoundly, to test hard generalizations to perturbations (aka perturbation testing), it will always be necessary that the perturbations are not trivially represented in the training data. Including perturbation trials during training would compromise our main finding: some biological model constraints improve the generalization to perturbation. To test this claim, it was necessary to keep the perturbations out of the training data.

We agree that including all available data of perturbed and non-perturbed recordings would be useful to build the best generalist predictive system. It could help, for instance, for closed-loop circuit control as we studied in Figure 5. Yet, there too, it will be important for the scientific validation process to always keep some causal perturbations of interest out of the training set. This is necessary to fairly measure the real generalization capability of any model. Importantly, this is why we think out-of-distribution “perturbation testing” is likely to have a recurring impact in the years to come, even beyond the case of optogenetic inactivation studied in detail in our paper.

Recommendation for the authors:

Reviewer #1 (Recommendation for the authors):

The code is not very easy to follow. I know this is a lot to ask, but maybe make clear where the code is to train the different models, which I think is a great contribution of this work? I predict that many readers will want to use the code and so this will improve the impact of this work.

We updated the code to make it easier to train a model from scratch.

Reviewer #2 (Recommendation for the authors):

The figures are really tough to read. Some of that small font should be sized up, and it's tough to tell in the posted paper what's happening in Figure 2B.

We updated Figures 1 and 2 significantly, in part to increase their readability. We also implemented the "Superficialities" suggestions.

Author response:

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

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

The authors analyzed the expression of ATAD2 protein in post-meiotic stages and characterized the localization of various testis-specific proteins in the testis of the Atad2 knockout (KO). By cytological analysis as well as the ATAC sequencing, the study showed that increased levels of HIRA histone chaperone, accumulation of histone H3.3 on post-meiotic nuclei, defective chromatin accessibility and also delayed deposition of protamines. Sperm from the Atad2 KO mice reduces the success of in vitro fertilization. The work was performed well, and most of the results are convincing. However, this manuscript does not suggest a molecular mechanism for how ATAD2 promotes the formation of testis-specific chromatin. 

We would like to take this opportunity to highlight that the present study builds on our previously published work, which examined the function of ATAD2 in both yeast S. pombe and mouse embryonic stem (ES) cells (Wang et al., 2021). In yeast, using genetic analysis we showed that inactivation of HIRA rescues defective cell growth caused by the absence of ATAD2. This rescue could also be achieved by reducing histone dosage, indicating that the toxicity depends on histone over-dosage, and that HIRA toxicity, in the absence of ATAD2, is linked to this imbalance.

Furthermore, HIRA ChIP-seq performed in mouse ES cells revealed increased nucleosome-bound HIRA, particularly around transcription start sites (TSS) of active genes, along with the appearance of HIRA-bound nucleosomes within normally nucleosome-free regions (NFRs). These findings pointed to ATAD2 as a major factor responsible for unloading HIRA from nucleosomes. This unloading function may also apply to other histone chaperones, such as FACT (see Wang et al., 2021, Fig. 4C).

In the present study, our investigations converge on the same ATAD2 function in the context of a physiologically integrated mammalian system—spermatogenesis. Indeed, in the absence of ATAD2, we observed H3.3 accumulation and enhanced H3.3-mediated gene expression. Consistent with this functional model of ATAD2— unloading chaperones from histone- and non-histone-bound chromatin—we also observed defects in histone-toprotamine replacement.

Together, the results presented here and in Wang et al. (2021) reveal an underappreciated regulatory layer of histone chaperone activity. Previously, histone chaperones were primarily understood as factors that load histones. Our findings demonstrate that we must also consider a previously unrecognized regulatory mechanism that controls assembled histone-bound chaperones. This key point was clearly captured and emphasized by Reviewer #2 (see below).

Strengths:

The paper describes the role of ATAD2 AAA+ ATPase in the proper localization of sperm-specific chromatin proteins such as protamine, suggesting the importance of the DNA replication-independent histone exchanges with the HIRA-histone H3.3 axis. 

Weaknesses: 

(1) Some results lack quantification. 

We will consider all the data and add appropriate quantifications where necessary.

(2) The work was performed well, and most of the results are convincing. However, this manuscript does not suggest a molecular mechanism for how ATAD2 promotes the formation of testis-specific chromatin. 

Please see our comments above.

Reviewer #2 (Public review): 

Summary:

This manuscript by Liakopoulou et al. presents a comprehensive investigation into the role of ATAD2 in regulating chromatin dynamics during spermatogenesis. The authors elegantly demonstrate that ATAD2, via its control of histone chaperone HIRA turnover, ensures proper H3.3 localization, chromatin accessibility, and histone-toprotamine transition in post-meiotic male germ cells. Using a new well-characterized Atad2 KO mouse model, they show that ATAD2 deficiency disrupts HIRA dynamics, leading to aberrant H3.3 deposition, impaired transcriptional regulation, delayed protamine assembly, and defective sperm genome compaction. The study bridges ATAD2's conserved functions in embryonic stem cells and cancer to spermatogenesis, revealing a novel layer of epigenetic regulation critical for male fertility. 

Strengths:

The MS first demonstration of ATAD2's essential role in spermatogenesis, linking its expression in haploid spermatids to histone chaperone regulation by connecting ATAD2-dependent chromatin dynamics to gene accessibility (ATAC-seq), H3.3-mediated transcription, and histone eviction. Interestingly and surprisingly, sperm chromatin defects in Atad2 KO mice impair only in vitro fertilization but not natural fertility, suggesting unknown compensatory mechanisms in vivo. 

Weaknesses:

The MS is robust and there are not big weaknesses 

Reviewer #3 (Public review): 

Summary: 

The authors generated knockout mice for Atad2, a conserved bromodomain-containing factor expressed during spermatogenesis. In Atad2 KO mice, HIRA, a chaperone for histone variant H3.3, was upregulated in round spermatids, accompanied by an apparent increase in H3.3 levels. Furthermore, the sequential incorporation and removal of TH2B and PRM1 during spermiogenesis were partially disrupted in the absence of ATAD2, possibly due to delayed histone removal. Despite these abnormalities, Atad2 KO male mice were able to produce offspring normally. 

Strengths:

The manuscript addresses the biological role of ATAD2 in spermatogenesis using a knockout mouse model, providing a valuable in vivo framework to study chromatin regulation during male germ cell development. The observed redistribution of H3.3 in round spermatids is clearly presented and suggests a previously unappreciated role of ATAD2 in histone variant dynamics. The authors also document defects in the sequential incorporation and removal of TH2B and PRM1 during spermiogenesis, providing phenotypic insight into chromatin transitions in late spermatogenic stages. Overall, the study presents a solid foundation for further mechanistic investigation into ATAD2 function. 

Weaknesses:

While the manuscript reports the gross phenotype of Atad2 KO mice, the findings remain largely superficial and do not convincingly demonstrate how ATAD2 deficiency affects chromatin dynamics. Moreover, the phenotype appears too mild to elucidate the functional significance of ATAD2 during spermatogenesis. 

We respectfully disagree with the statement that our findings are largely superficial. Based on our investigations of this factor over the years, it has become evident that ATAD2 functions as an auxiliary factor that facilitates mechanisms controlling chromatin dynamics (see, for example, Morozumi et al., 2015). These mechanisms can still occur in the absence of ATAD2, but with reduced efficiency, which explains the mild phenotype we observed.

This function, while not essential, is nonetheless an integral part of the cell’s molecular biology and should be studied and brought to the attention of the broader biological community, just as we study essential factors. Unfortunately, the field has tended to focus primarily on core functional actors, often overlooking auxiliary factors. As a result, our decade-long investigations into the subtle yet important roles of ATAD2 have repeatedly been met with skepticism regarding its functional significance, which has in turn influenced editorial decisions.

We chose eLife as the venue for this work specifically to avoid such editorial barriers and to emphasize that facilitators of essential functions do exist. They deserve to be investigated, and the underlying molecular regulatory mechanisms must be understood.

(1) Figures 4-5: The analyses of differential gene expression and chromatin organization should be more comprehensive. First, Venn diagrams comparing the sets of significantly differentially expressed genes between this study and previous work should be shown for each developmental stage. Second, given the established role of H3.3 in MSCI, the effect of Atad2 knockout on sex chromosome gene expression should be analyzed. Third, integrated analysis of RNA-seq and ATAC-seq data is needed to evaluate how ATAD2 loss affects gene expression. Finally, H3.3 ChIP-seq should be performed to directly assess changes in H3.3 distribution following Atad2 knockout.  

(1) In the revised version, we will include Venn diagrams to illustrate the overlap in significantly differentially expressed genes between this study and previous work. However, we believe that the GSEAs presented here provide stronger evidence, as they indicate the statistical significance of this overlap (p-values). In our case, we observed p-value < 0.01 (**) and p < 0.001 (***).

(2) Sex chromosome gene expression was analyzed and is presented in Fig. 5C.

(3) The effect of ATAD2 loss on gene expression is shown in Fig. 4A, B, and C as histograms, with statistical significance indicated in the middle panels.

(4) Although mapping H3.3 incorporation across the genome in wild-type and Atad2 KO cells would have been informative, the available anti-H3.3 antibody did not work for ChIP-seq, at least in our hands. The authors of Fontaine et al., 2022, who studied H3.3 during spermatogenesis in mice, must have encountered the same problem, since they tagged the endogenous H3.3 gene to perform their ChIP experiments.

(2) Figure 3: The altered distribution of H3.3 is compelling. This raises the possibility that histone marks associated with H3.3 may also be affected, although this has not been investigated. It would therefore be important to examine the distribution of histone modifications typically associated with H3.3. If any alterations are observed, ChIP-seq analyses should be performed to explore them further.

Based on our understanding of ATAD2’s function—specifically its role in releasing chromatin-bound HIRA—in the absence of ATAD2 the residence time of both HIRA and H3.3 on chromatin increases. This results in the detection of H3.3 not only on sex chromosomes but across the genome. Our data provide clear evidence of this phenomenon. The reviewer is correct in suggesting that the accumulated H3.3 would carry H3.3-associated histone PTMs; however, we are unsure what additional insights could be gained by further demonstrating this point.

(3) Figure 7: While the authors suggest that pre-PRM2 processing is impaired in Atad2 KO, no direct evidence is provided. It is essential to conduct acid-urea polyacrylamide gel electrophoresis (AU-PAGE) followed by western blotting, or a comparable experiment, to substantiate this claim. 

Figure 7 does not suggest that pre-PRM2 processing is affected in Atad2 KO; rather, this figure—particularly Fig. 7B—specifically demonstrates that pre-PRM2 processing is impaired, as shown using an antibody that recognizes the processed portion of pre-PRM2. ELISA was used to provide a more quantitative assessment; however, in the revised manuscript we will also include a western blot image.

(4) HIRA and ATAD2: Does the upregulation of HIRA fully account for the phenotypes observed in Atad2 KO? If so, would overexpression of HIRA alone be sufficient to phenocopy the Atad2 KO phenotype? Alternatively, would partial reduction of HIRA (e.g., through heterozygous deletion) in the Atad2 KO background be sufficient to rescue the phenotype? 

These are interesting experiments that require the creation of appropriate mouse models, which are not currently available.

(5) The mechanism by which ATAD2 regulates HIRA turnover on chromatin and the deposition of H3.3 remains unclear from the manuscript and warrants further investigation. 

The Reviewer is absolutely correct. In addition to the points addressed in response to Reviewer #1’s general comments (see above), it would indeed have been very interesting to test the segregase activity of ATAD2 (likely driven by its AAA ATPase activity) through in vitro experiments using the Xenopus egg extract system described by Tagami et al., 2004. This system can be applied both in the presence and absence (via immunodepletion) of ATAD2 and would also allow the use of ATAD2 mutants, particularly those with inactive AAA ATPase or bromodomains. However, such experiments go well beyond the scope of this study, which focuses on the role of ATAD2 in chromatin dynamics during spermatogenesis.

References:

(1) Wang T, Perazza D, Boussouar F, Cattaneo M, Bougdour A, Chuffart F, Barral S, Vargas A, Liakopoulou A, Puthier D, Bargier L, Morozumi Y, Jamshidikia M, Garcia-Saez I, Petosa C, Rousseaux S, Verdel A, Khochbin S. ATAD2 controls chromatin-bound HIRA turnover. Life Sci Alliance. 2021 Sep 27;4(12):e202101151. doi: 10.26508/lsa.202101151. PMID: 34580178; PMCID: PMC8500222.

(2) Morozumi Y, Boussouar F, Tan M, Chaikuad A, Jamshidikia M, Colak G, He H, Nie L, Petosa C, de Dieuleveult M, Curtet S, Vitte AL, Rabatel C, Debernardi A, Cosset FL, Verhoeyen E, Emadali A, Schweifer N, Gianni D, Gut M, Guardiola P, Rousseaux S, Gérard M, Knapp S, Zhao Y, Khochbin S. Atad2 is a generalist facilitator of chromatin dynamics in embryonic stem cells. J Mol Cell Biol. 2016 Aug;8(4):349-62. doi: 10.1093/jmcb/mjv060. Epub 2015 Oct 12. PMID: 26459632; PMCID: PMC4991664.

(3) Fontaine E, Papin C, Martinez G, Le Gras S, Nahed RA, Héry P, Buchou T, Ouararhni K, Favier B, Gautier T, Sabir JSM, Gerard M, Bednar J, Arnoult C, Dimitrov S, Hamiche A. Dual role of histone variant H3.3B in spermatogenesis: positive regulation of piRNA transcription and implication in X-chromosome inactivation. Nucleic Acids Res. 2022 Jul 22;50(13):7350-7366. doi: 10.1093/nar/gkac541. PMID: 35766398; PMCID: PMC9303386.

(4) Tagami H, Ray-Gallet D, Almouzni G, Nakatani Y. Histone H3.1 and H3.3 complexes mediate nucleosome assembly pathways dependent or independent of DNA synthesis. Cell. 2004 Jan 9;116(1):51-61. doi: 10.1016/s0092-8674(03)01064-x. PMID: 14718166.

Recommendations for the authors:

Reviewing Editor Comments:

I note that the reviewers had mixed opinions about the strength of the evidence in the manuscript. A revision that addresses these points would be welcome.

Reviewer #1 (Recommendations for the authors):  

Major points: 

(1) No line numbers: It is hard to point out the issues.

The revised version harbors line numbers.

(2) Given the results shown in Figure 3 and Figure 4, it is nice to show the chromosomal localization of histone H3.3 in spermatocytes or post-meiotic cells by Chromatin-immunoprecipitation sequencing (ChIP-seq).

Although mapping H3.3 incorporation across the genome in wild-type and Atad2 KO cells would have been informative, the available anti-H3.3 antibody did not work for ChIP-seq in our hands. In fact, this antibody is not well regarded for ChIP-seq. For example, Fontaine et al. (2022), who investigated H3.3 during spermatogenesis in mice, circumvented this issue by tagging the endogenous H3.3 genes for their ChIP experiments.

(3) Figure 7B and 8: Why the authors used ELISA for the protein quantification. At least, western blotting should be shown.

ELISA is a more quantitative method than traditional immunoblotting. Nevertheless, as requested by the reviewer, we have now included a corresponding western blot in Fig. S3.

(4) For readers, please add a schematic pathway of histone-protamine replacement in sperm formation in Fig.1 and it would be nice to have a model figure, which contains the authors' idea in the last figure.

As requested by this reviewer, we have now included a schematic model in Figure 9 to summarize the main conclusions of our work.

Minor points: 

(1) Page 2, the second paragraph, "pre-PRM2: Please explain more about pre-PRM2 and/or PRM2 as well as PRM1 (Figure 6).

More detailed descriptions of PRM2 processing are now given in this paragraph. 

(2) Page 3, bottom paragraph, line 1: "KO" should be "knockout (KO)".

Done.

(3) Page 4, second paragraph bottom: Please explain more about the protein structure of germ-line-specific ATAD2S: how it is different from ATAD2L. Germ-line specific means it is also expressed in ovary?

As Atad2 is predominantly expressed in embryonic stem cells and in spermatogenic cells, we replaced all through the text germ-line specific by more appropriate terms.

(4) Figure 1C, western blotting: Wild-type testis extracts, both ATAD2L and -S are present. Does this mean that ATADS2L is expressed in both germ line as well as supporting cells. Please clarify this and, if possible, show the western blotting of spermatids well as spermatocytes.

Figure 1D shows sections of seminiferous tubules from Atad2 KO mice, in which lacZ expression is driven by the endogenous Atad2 promoter. The results indicate that Atad2 is expressed mainly in post-meiotic cells. Most labeled cells are located near the lumen, whereas the supporting Sertoli cells remain unlabeled. Sertoli cells, which are anchored to the basal lamina, span the entire thickness of the germinal epithelium from the basal lamina to the lumen. Their nuclei, however, are usually positioned closer to the basal membrane. Thus, the observed lacZ expression pattern argues against substantial Atad2 expression in Sertoli cells. 

(5) Figure 1C: Please explain a bit more about the reduction of ATAD2 proteins in heterozygous mice.

Done

(6) Figure 1C: Genotypes of the mice should be shown in the legend.

Done 

(7) Figure 1D: Please add a more magnified image of the sections to see the staining pattern in the seminiferous tubules.

The magnification does not bring more information since we lose the structure of cells within tubules due the nature of treatment of the sections for X-gal staining. Please see comments to question 1C to reviewer 2

(8) Page 5, first paragraph, line 2, histone dosage: What do the authors meant by the histone dosage? Please explain more or use more appropriate word.

"Histone dosage" refers to the amount or relative abundance of histone proteins in a cell.

(9) Figure 2A: Figure 2A: Given the result in Figure 1C, it is interesting to check the amount of HIRA in Atad2 heterozygous mice.

In Atad2 heterozygous mice, we would expect an increase in HIRA, but only to about half the level seen in the Atad2 homozygous knockout shown in Figure 2A, which is relatively modest. Therefore, we doubt that detecting such a small change—approximately half of that in Figure 2A—would yield clear or definitive results. 

(10) Figure 2A, legend (n=5): What does this "n" mean? The extract of testes from "5" male mice like Figure 2B. Or 5 independent experiments. If the latter is true, it is important to share the other results in the Supplements.

“n” refers to five WT and five Atad2 KO males. The legend has been clarified as suggested by the reviewer.

(11) Figure 2A, legend, line 2, Atad2: This should be italicized.

Done

(12) Figure 2B: Please show the quantification of amounts of HIRA protein like Fig. 2A.

As indicated in the legend, what is shown is a pool of testes from 3 individuals per genotype.

(13) Figure 2B shows an increased level of HIRA in Atad2 KO testis. This suggests the role of ATAD2 in the protein degradation of HIRA. This possibility should be mentioned or tested since ATAD2 is an AAA+ ATPase. 

The extensive literature on ATAD2 provides no indication that it is involved in protein degradation. In our early work on ATAD2 in the 2000s, we hypothesized that, as a member of the AAA ATPase family, ATAD2 might associate with the 19S proteasome subunit (through multimerization with the other AAA ATPase member of this regulatory subunit). However, both our published pilot studies (Caron et al., PMID: 20581866) and subsequent unpublished work ruled out this possibility. Instead, since the amount of nucleosome-bound HIRA increases in the absence of ATAD2, we propose that chromatin-bound HIRA is more stable than soluble HIRA once it has been released from chromatin by ATAD2.

(14) Page 6, second paragraph, line 5, ko: KO should be capitalized.

Done

(15) Page 6, second paragraph, line 2 from the bottom, chromatin dynamics: Throughout the text, the authors used "chromatin dynamics". However, all the authors analyzed in the current study is the localization of chromatin protein.  So, it is much easier to explain the results by using "chromatin status," etc. In this context, "accessibility" is better. 

We changed the term “chromatin dynamics” into a more precise term according to the context used all through the text.

(16) Figure 3: Please provide the quantification of signals of histone H3.3 in a nucleus or nuclear cytoplasm.

This request is not clear to us since we do not observe any H3.3 signal in the cytoplasm.

(17) Figure 3: As the control of specificity in post-meiotic cells, please show the image and quantification of the H3.3 signals in spermatocyte, for example.

This request is not clear to us. What specificity is meant? 

(18) Figure 3, bottom panels: Please show what the white lines indicate? 

The white lines indicate the limit of cell nucleus and estimated by Hoechst staining. This is now indicated in the legend of the figure. 

(19) Figure 4A: Please explain more about what kind of data is here. Is this wild-type and/or Atad2 KO? The label of the Y-axis should be "mean expression level". What is the standard deviation (SD) here on the X-axis. Moreover, there is only one red open circle, but the number of this class is 5611. All 5611 genes in this group show NO expression. Please explain more.

The plot displays the mean expression levels (y-axis, labeled as "mean expression level") versus the corresponding standard deviations (x-axis), both calculated from three independent biological replicates of isolated round spermatids (Atad2 wild-type and Atad2 KO). The standard deviation reflects the variability of gene expression across biological replicates. Genes were grouped into four categories (grp1: blue, grp2: cyan, grp3: green, grp4: orange) according to the quartile of their mean expression. For grp4, all genes have no detectable expression, resulting in a mean expression of zero and a standard deviation of zero; consequently, the 5611 genes in this group are represented by a single overlapping point (red open circle) at the origin. 

(20) Figure 4C: If possible, it would be better to have a statistical comparison between wild-type and the KO.  

The mean profiles are displayed together with their variability (± 2 s.e.m.) across the four replicates for both ATAD2 WT (blue) and ATAD2 KO (red). For groups 1, 2, and 3, the envelopes of the curves remain clearly separated around the peak, indicating a consistent difference in signal between the two conditions. In contrast, group 4 does not present a strong signal and, accordingly, no marked difference is observed between WT and KO in this group.

(21) Figure 5, GSEA panels: Please explain more about what the GSEA is in the legend.  The legend has been updated as follows:

(A) Expression profiles of post-meiotic H3.3-activated genes. The heatmap (left panel) displays the normalized expression levels of genes identified by Fontaine and colleagues as upregulated in the absence of histone H3.3 (Fontaine et al. 2022) for Atad2 WT (WT) and Atad2 KO (KO) samples at days 20, 22, 24, and 26 PP (D20 to D26). The colour scale represents the z-score of log-transformed DESeq2-normalized counts. The middle panel box plots display, pooled, normalized expression levels, aggregated across replicates and genes, for each condition (WT and KO) and each time point (D20 to D26). Statistical significance between WT and KO conditions was determined using a two-sided t-test, with p-values indicated as follows: * for p-value<0.05, ** for p-value<0.01 and *** for p-value<0.001. The right panel shows the results of gene set enrichment analysis (GSEA), which assesses whether predefined groups of genes show statistically significant differences between conditions. Here, the post-meiotic H3.3-activated genes set, identified by Fontaine et al. (2022), is significantly enriched in Atad2 KO compared with WT samples at day 26 (p < 0.05, FDR < 0.25). Coloured vertical bars indicate the “leading edge” genes (i.e., those contributing most to the enrichment signal), located before the point of maximum enrichment score.  (B) As shown in (A) but for the "post-meiotic H3.3-repressed genes" gene set. (C) As shown in (A) but for the " sex chromosome-linked genes " gene set.

(22) Figure 6. In the KO, the number of green cells is more than red and yellow cells, suggesting the delayed maturation of green (TH2B-positive) cells. It is essential to count the number of each cell and show the quantification.

The green cells correspond to those expressing TH2B but lacking transition proteins (TP) and protamine 1 (Prm1), indicating that they are at earlier stages than elongating–condensing spermatids. Counting these green cells simply reflects the ratio of elongating/condensing spermatids to earlier-stage cells, which varies depending on the field examined. The key point in this experiment is that in wild-type mice, only red cells (elongating/condensing spermatids) and green cells (earlier stages) are observed. By contrast, in Atad2 KO testes, a significant proportion of yellow cells appears, which are never seen in wild-type tissue. The crucial metric here is the percentage of yellow cells relative to the total number of elongating/condensing spermatids (red cells). In wild-type testes, this value is consistently 0%, whereas in Atad2 KO testes it always ranges between 50% and 100% across all fields containing substantial numbers of elongating/condensing spermatids.

(23) Figure 8A: Please show the images of sperm (heads) in the KO mice with or without decompaction.

The requested image is now displayed in Figure S5.

(24) Figure 8C: In the legend, it says n=5. However, there are more than 5 plots on the graph. Please explain the experiment more in detail.

The experiment is now better explained in the legend of this Figure.

Reviewer #2 (Recommendations for the authors): 

While the study is rigorous and well performed, the following minor points could be addressed to strengthen the manuscript: 

Figure 1C should indicate each of the different types of cells present in the sections. It would be of interest to show specifically the different post-meiotic germ cells.

With this type of sample preparation, it is difficult to precisely distinguish the different cell types within the sections. Nevertheless, the staining pattern strongly indicates that most of the intensely stained cells are post-meiotic, situated near the tubule lumens and extending roughly halfway toward the basal membrane.

In the absence of functional ATAD2, the accumulation of HIRA primarily occurs in round spermatids (Fig. 2B). If technically possible, it would be of great interest to show this by IHC of testis section. 

Unfortunately, our antibody did not satisfactorily work in IHC.

The increased of H3.3 signal in Atad2 KO spermatids (Fig. 3) is interpreted because of a reduced turnover. However, alternative explanations (e.g., H3.3 misincorporation or altered chaperone affinity) should not be ruled out. 

The referee is correct that alternative explanations are possible. However, based on our previous work (Wang et al., 2021; PMID: 34580178), we demonstrated that in the absence of ATAD2, there is reduced turnover of HIRAbound nucleosomes, as well as reduced nucleosome turnover, evidenced by the appearance of nucleosomes in regions that are normally nucleosome-free at active gene TSSs. We have no evidence supporting any other alternative hypothesis.

In the MS the reduced accessibility at active genes (Fig. 4) is attributed to H3.3 overloading. However, global changes in histone acetylation (e.g., H4K5ac) or other remodelers in KO cells could be also consider.

In fact, we meant that histone overloading could be responsible for the altered accessibility. This has been clearly demonstrated in case of S. cerevisiae in the absence of Yta7 (S.  cerevisiae’ ATAD2) (PMID: 25406467).

In relation with the sperm compaction assay (Fig. 8A), the DTT/heparin/Triton protocol may not fully reflect physiological decompaction. This could be validated with alternative methods (e.g., MNase sensitivity). 

The referee is right, but since this is a subtle effect as it can be judged by normal fertility, we doubt that milder approaches could reveal significant differences between wildtype and Atad2 KO sperms.

It is surprising that despite the observed alterations in the genome organization of the sperm, the natural fertility of the KO mice is not affected (Fig. 8C). This warrants deeper discussion: Is functional compensation occurring (e.g., by p97/VCP)? Analysis of epididymal sperm maturation or uterine environment could provide insights.

As detailed in the Discussion section, this work, together with our previous study (Wang et al., 2021; PMID: 34580178), highlights an overlooked level of regulation in histone chaperone activity: the release of chromatinbound factors following their interaction with chromatin. This is an energy-dependent process, driven by ATP and the associated ATPase activity of these factors. Such activity could be mediated by various proteins, such as p97/VCP or DNAJC9–HSP70, as discussed in the manuscript, or by yet unidentified factors. However, most of these mechanisms are likely to occur during the extensive histone-to-histone variant exchanges of meiosis and post-meiotic stages. To the best of our knowledge, epididymal sperm maturation and the uterine environment do not involve substantial histone-to-histone or histone-to-protamine exchanges.

The authors showed that MSCI genes present an enhancement of repression in the absence of ATAD2 by enhancing H3.3 function. It would be also of interest to analyze the behavior of the Sex body during its silencing (zygotene to pachytene) by looking at different markers (i.e., gamma-H2AX phosphorylation, Ubiquitylation etc). 

The referee is correct that this is an interesting question. Accordingly, in our future work, we plan to examine the sex body in more detail during its silencing, using a variety of relevant markers, including those suggested by the reviewer. However, we believe that such investigations fall outside the scope of the present study, which focuses on the molecular relationship between ATAD2 and H3.3, rather than on the role of H3.3 in regulating sex body transcription. For a comprehensive analysis of this aspect, studies should primarily focus on the H3.3 mouse models reported by Fontaine and colleagues (PMID: 35766398).

Fig. 6: Co-staining of TH2B/TP1/PRM1 is convincing but would benefit from quantification (% cells with overlapping signals).

The green cells correspond to those expressing TH2B but lacking transition proteins (TP) and protamine 1 (Prm1), indicating that they are at earlier stages than elongating–condensing spermatids. Counting these green cells simply reflects the ratio of elongating/condensing spermatids to earlier-stage cells, which varies depending on the field examined. The key point is that in wild-type mice, only red cells (elongating/condensing spermatids) and green cells (earlier stages) are observed. By contrast, in Atad2 KO testes, a significant proportion of yellow cells appears, which are never seen in wild-type tissue. The crucial metric is the percentage of yellow cells relative to the total number of elongating/condensing spermatids (red cells). In wild-type testes, this value is consistently 0%, whereas in Atad2 KO testes it always ranges between 50% and 100% across all fields containing substantial numbers of elongating/condensing spermatids.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

In the manuscript by Fu et al., the authors developed a chemo-immunological method for the reliable detection of Kacac, a novel post-translational modification, and demonstrated that acetoacetate and AACS serve as key regulators of cellular Kacac levels. Furthermore, the authors identified the enzymatic addition of the Kacac mark by acyltransferases GCN5, p300, and PCAF, as well as its removal by deacetylase HDAC3. These findings indicate that AACS utilizes acetoacetate to generate acetoacetyl-CoA in the cytosol, which is subsequently transferred into the nucleus for histone Kacac modification. A comprehensive proteomic analysis has identified 139 Kacac sites on 85 human proteins. Bioinformatics analysis of Kacac substrates and RNA-seq data reveal the broad impacts of Kacac on diverse cellular processes and various pathophysiological conditions. This study provides valuable additional insights into the investigation of Kacac and would serve as a helpful resource for future physiological or pathological research.

The authors have made efforts to revise this manuscript and address my concerns. The revisions are appropriate and have improved the quality of the manuscript.

We appreciate the constructive and thoughtful feedbacks, which have been invaluable in enhancing the quality of our manuscript.

Reviewer #3 (Public review):

Summary:

This paper presents a timely and significant contribution to the study of lysine acetoacetylation (Kacac). The authors successfully demonstrate a novel and practical chemoimmunological method using the reducing reagent NaBH4 to transform Kacac into lysine βhydroxybutyrylation (Kbhb).

Thank you for the positive and insightful comments.

Strengths:

This innovative approach enables simultaneous investigation of Kacac and Kbhb, showcasing its potential in advancing our understanding of post-translational modifications and their roles in cellular metabolism and disease.

We are grateful for the reviewer’s comments, which has contributed to enhancing the quality of our study.

Weaknesses:

The experimental evidence presented in the article is insufficient to fully support the authors' conclusions. In the in vitro assays, the proteins used appear to be highly inconsistent with their expected molecular weights, as shown by Coomassie Brilliant Blue staining (Figure S3A). For example, p300, which has a theoretical molecular weight of approximately 270 kDa, appeared at around 37 kDa; GCN5/PCAF, expected to be ~70 kDa, appeared below 20 kDa. Other proteins used in the in vitro experiments also exhibited similarly large discrepancies from their predicted sizes. These inconsistencies severely compromise the reliability of the in vitro findings. Furthermore, the study lacks supporting in vivo data, such as gene knockdown experiments, to validate the proposed conclusions at the cellular level.

We appreciate the reviewer’s comments. In the biochemical assays, we used the expressed catalytic domains of HATs—rather than the full-length proteins for activity testing. Specifically, the following constructs were expressed and purified: p300 (1287– 1666), GCN5 (499-663), PCAF (493-658), MOF (125-458), MOZ (497-780), MBP-MORF (361-716), Tip60 (221-512), HAT1 (20-341), and HBO1 (full length). This resulted in the observed discrepancies in molecular weight in Figure S3A compared to the expected fulllength weights. 

Although a recent study (PMID: 37382194) reported the acetoacetyltransferase activities of p300 and GCN5 in cells, we recognize that additional knockdown experiments would be necessary to substantiate their contributions to in vivo Kacac generation and to explore the functional roles of Kacac in an enzyme-specific context. We plan to address these kinds of research issues in our future work.

Author response:

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

Public Reviews:

Reviewer #1 (Public review)

The Cx3cr1/EGFP line labels all myeloid cells, which makes it difficult to conclude that all observed behaviors are attributable to microglia rather than infiltrating macrophages. The authors refer to this and include it as a limitation. Nonetheless, complementary confirmation by additional microglia markers would strengthen their claims. 

We appreciate the reviewer’s insightful comment regarding the cellular identity of the enveloping myeloid cells. As suggested, we performed triple co-immunostaining of SSLOW-infected Cx3cr1/EGFP mice using markers for neurons (NeuN), myeloid cells (IBA1), and resident microglia (TMEM119 or P2Y12). Because formic acid treatment used to deactivate prions abolishes the EGFP signal, we relied on IBA1 staining to identify the myeloid population. Our results confirmed that IBA1⁺ cells exhibiting the envelopment behavior are also TMEM119⁺ and P2Y12⁺, consistent with a resident microglial phenotype. These new data are presented in Figures S3 and S4 and described in the final section of the Results.

Although the authors elegantly describe dynamic surveillance and envelopment hypothesis, it is unclear what the role of this phenotype is for disease progression, i.e., functional consequences. For example, are the neurons that undergo sustained envelopment more likely to degenerate? 

We appreciate this important question regarding the functional implications of neuronal envelopment. At present, technical limitations prevent us from continuously tracking the fate of individual enveloped neurons in prion-infected mice. Nevertheless, our recent study demonstrated that P2Y12 knockout increases the prevalence of neuronal envelopment and accelerates disease progression (Makarava et al., 2025, J. Neuroinflammation). These findings suggest that while microglial envelopment may represent an adaptive response to increased neuronal surveillance demands, excessive envelopment, as observed in the absence of P2Y12, appears to be maladaptive. A new paragraph has been added to the Discussion to address this point.

Moreover, although the increase in mobility is a relevant finding, it would be interesting for the authors to further comment on what the molecular trigger(s) is/are that might promote this increase. These adaptations, which are at least long-lasting, confer apparent mobility in the absence of external stimuli. 

We thank the reviewer for this thoughtful suggestion. The molecular mechanisms underlying the increased mobility of microglia in prion-infected brains remain to be identified, and we plan to pursue this question in future studies. One possibility we briefly discuss in the revised manuscript is that proinflammatory signaling, mediated by secreted cytokines or interleukins, may drive this phenotype. Supporting this hypothesis, recent work has shown that IFNγ enhances microglial migration in the adult mouse cortex (doi:10.1073/pnas.2302892120). This work has been cited in the revised manuscript.

The authors performed, as far as I could understand, the experiments in cortical brain regions. There is no clear rationale for this in the manuscript, nor is it clear whether the mobility is specific to a particular brain region. This is particularly important, as microglia reactivity varies greatly depending on the brain region. 

We appreciate this insightful comment highlighting the importance of regional determinants of microglial reactivity, which indeed aligns with our ongoing research interests. In our previous studies, neuronal envelopment by microglia was observed consistently across all prion-affected brain regions exhibiting neuroinflammation. Assuming that envelopment requires microglial mobility, it is reasonable to speculate that microglia are mobile in all brain regions affected by prions and displaying neuroinflammatory responses. In the current study, we focused exclusively on the cortex because this region was used for quantifying the prevalence of neuronal envelopment as a function of disease progression in our prior work (DOI: 10.1172/JCI181169), which guided the present study design. Our ongoing investigations indicate that the prevalence of envelopment is region-dependent and correlates with microglial reactivity/the degree of neuroinflammation. In prion diseases, the degree of microglial reactivity is dictated by the tropism of specific prion strains to distinct brain regions. Notably, our prior studies have shown that strain-specific sialylation patterns of PrP^Sc glycans play a key role in determining both regional strain tropism and the extent of neuroinflammatory activation (DOI: 10.3390/ijms21030828, DOI: 10.1172/JCI138677). In response to this comment, we have added a brief rationale for using the cortex in the Results section.

It would be relevant information to have an analysis of the percentage of cells in normal, sub-clinical, early clinical, and advanced stages that became mobile. Without this information, the speed/distance alone can have different interpretations.

We thank the reviewer for this valuable suggestion. The percentage of mobile cells across normal, sub-clinical, early clinical, and advanced disease stages is presented in Figure 3b and described in the final paragraph of the section “Enveloping behavior of reactive myeloid cells.”

Reviewer #2 (Public review)

The number of individual cells tracked has been provided, but not the number of individual mice. The sex of the mice is not provided. 

We used N = 3 animals per group throughout the study; this information has now been added to the figure legends. Animals of both sexes were included in random proportions. The sex information is now listed for each experiment in the Animals subsection of the Methods.

The statistical approach is not clear; was each cell treated as a single observation? 

Yes, with the exception of the heat map in Figure 2d, all mobility parameters are analyzed and presented at the level of individual cells, with each cell treated as an independent observation. The primary aim of this study is to characterize behavioral patterns of single reactive myeloid cells. Analyzing data at the cell level allows us to capture the full distribution of cell behaviors and to preserve biologically meaningful heterogeneity within and across animals. By contrast, averaging values per animal would largely mask this variability. In the heat map in Figure 2d, data are averaged per animal, specifically to illustrate inter-animal variability within each group and to visualize changes across disease progression.

The potential for heterogeneity among animals has not been addressed. 

To address this concern, we now include a new Supplemental Figure (Figure S4)  presenting the data using Superplots, in which individual cells are shown as dots, animal-level average as circles, and group means calculated based on animals as black horizontal lines. These plots demonstrate that cell mobility measures are highly consistent across animals within each group, indicating limited inter-animal heterogeneity.

Validation of prion accumulation at each clinical stage of the disease is not provided. 

We now provide validation of PrP^Sc accumulation across disease stages by Western blot, along with quantitative analysis, in a new Supplemental Figure (Figure S2). This confirms progressive PrP^Sc accumulation with advancing disease.

How were the numerous captures of cells handled to derive morphological quantitative values? Based on the videos, there is a lot of movement and shape-shifting.

The following description has been added to Methods to clarify morphology analysis: For microglial morphology analysis, we quantified morphological parameters (radius, area, perimeter, and shape index) for individual EGFP⁺ cells in each time frame of the time-lapse recordings using the TrackMate 7.13.2 plugin in FIJI. Parameter values for each cell were then averaged across the entire three-hour imaging period to obtain a single mean value per cell.

While it is recognized that there are limits to what can be measured simultaneously with live imaging, the authors appear to have fixed tissues from each time point too - it would be very interesting to know if the extent or prion accumulation influences the microglial surveillance - i.e., do the enveloped ones have greater pathology. 

This is very interesting question which is difficult to answer due to technical challenges in monitoring the pathology or faith of individual neuronal cells as a function of their envelopment in live prion-infected animals. Our previous work revealed that both accumulation of total PrP^Sc in a brain and  accumulation of PrP^Sc specifically in lysosomal compartments of microglia due to phagocytosis precedes the onset of neuronal envelopment (DOI: 10.1172/JCI181169).  Moreover, the onset of neuronal envelopment occurred after a noticeable decline in neuronal levels of Grin1, a subunit of the NMDA receptor essential for synaptic plasticity. Reactive microglia were observed to envelop Grin1-deficient neurons, suggesting that microglia respond to neuronal dysfunction. However, considering that envelopment is very dynamic and - in most cases - reversible, correlating the degree of envelopment with dysfunction of individual neurons is technically challenging.

Recommendations for the authors

Reviewer #1 (Recommendations for the authors): 

(1) I recommend performing additional immunostaining using microglial markers to address specificity. 

These new data showing immunostaining for markers of resident microglia TMEM119 and P2Y12 are presented in Figures S6 and S7 and described in the final section of the Results.

(2) The authors can at least further discuss the functional consequences of their findings in further detail. 

A new paragraph has been added to the Discussion to address this point.

(3) Quantify the % of cells that become mobile in the different conditions. 

The percentage of mobile cells across normal, sub-clinical, early clinical, and advanced disease stages is presented in Figure 3b and described in the final paragraph of the section “Enveloping behavior of reactive myeloid cells.”

(4) Improve method details on the brain regions used and further expand the statistical section. 

We have expanded the Statistical Analysis section to indicate whether statistical comparisons and mean values were calculated at the single-cell level or the animal level for each analysis. The specific statistical tests used and the number of animals (N) are now reported in the corresponding figure legends. The sex of animals is provided in Table 1 (Methods). Only the cortical region was examined in this study; this information is stated in the Methods and is now also noted in the figure legends for clarity.

Reviewer #2 (Recommendations for the authors): 

(1) More details on members of the PY2 receptor family expressed in microglia would be helpful. The study highlights a previously published prion-induced decline in the expression of P2Y12, a microglial marker that is required for intracellular neuron-microglial contacts, and P2Y6, involved in calcium transients, which is required for hypermotility. How are members of this family of receptors regulated at the gene and/or protein level in microglial and given their responsiveness to nucleotide ligands, are other members implicated in the properties being quantified here? 

We appreciate the reviewer’s insightful comment. To address this point, we examined the expression of multiple P2Y receptors and ATP-gated P2X channels known to contribute to microglial surveillance, activation, motility, and phagocytosis, alongside the activation markers Tlr2, Cd68, and Trem2. Bulk brain transcript analyses indicated that all examined genes were upregulated in SSLOW-infected mice relative to controls (new Figure S5a). However, because microglial proliferation substantially increases microglial numbers during prion disease progression, bulk tissue measurements do not necessarily reflect per-cell expression levels. Therefore, we normalized gene expression values to the microglia-specific marker Tmem119, whose per-cell expression remains stable across disease stages (Makarava et al., 2025, J. Neuroinflammation). After normalization, Tlr2, Cd68, and Trem2 were increased approximately 10-, 6-, and 4-fold, respectively. In contrast, P2 receptor genes showed more modest changes: P2ry6 increased ~3-fold, P2ry13 ~2-fold, and P2rx7 ~1.3-fold, while P2rx4 remained unchanged (Figure S5a). Within the scope of the present study, we focused on P2Y6 due to (i) its role in regulating calcium transients, (ii) the magnitude of its upregulation relative to other P2 receptors, and (iii) its highly microglia-specific expression in the CNS. We note that currently available commercial P2Y6 antibodies lack sufficient specificity, making reliable assessment of protein-level expression challenging.

(2) Is P2Y6 expressed in any other cell type that might account for the blunted mobility of the microglia? The authors mention P2Y12 also identifies the GFP cells; however, it would be beneficial to highlight the specificity of the target in the ex vivo treatment of the infected slices.

In the brain, both P2Y12 and P2Y6 are considered highly specific to resident microglia under physiological and neuroinflammatory conditions. P2Y12 is, in fact, widely used as a canonical marker of homeostatic and resident microglia. While P2Y6 is also expressed in peripheral myeloid cells such as macrophages, our phenotypic characterization indicates that the cells exhibiting neuronal envelopment are TMEM119⁺ and P2Y12⁺, consistent with a resident microglial identity. These data, including new analyses added to the revised manuscript, support that the cells responding to P2Y6 signaling in our ex vivo slice experiments are resident microglia.

(3) The fluorescent mouse lacks Cx3cr1 - have the authors investigated why there were no apparent consequences, at least in the context of prion infection? Are there functional redundancies that might be harnessed? Does this impact the generalizability of the findings here?

The role of Cx3cr1 in prion disease has been directly examined in two independent studies (doi: 10.1099/jgv.0.000442; doi: 10.1186/1471-2202-15-44). One study reported no effect of Cx3cr1 deficiency on disease incubation time, whereas the other observed only a minor difference. Importantly, both studies found no detectable alterations in microglial activation patterns, cytokine expression, or PrP^Sc deposition in Cx3cr1-deficient mice compared to wild-type controls. Our own data (Figure S1) are consistent with these findings: disease course and PrP^Sc deposition were comparable between Cx3cr1/EGFP and wild-type mice. Moreover, we observed reactive microglial envelopment of neurons in both genotypes. Microglia isolated from SSLOW-infected Cx3cr1/EGFP mice also displayed similarly elevated mobility in vitro, in agreement with our previous observations of high mobility of microglia isolated from SSLOW-infected wild-type mice (Makarava et al., 2025, J. Neuroinflammation). Taken together, these results indicate that Cx3cr1 is not a key determinant of reactive microglial mobility or envelopment behavior in prion disease. Thus, the use of the Cx3cr1/EGFP reporter line does not compromise the generalizability of our conclusions.

(4) The distinction between high mobility and low mobility microglia is interesting - is there any evidence to suggest that the slow-moving microglia are actually a separate class - do enveloping microglia exhibit both mobility states - can the authors comment on plasticity here? 

We appreciate this insightful comment, which closely aligns with our ongoing interests. At present, we do not have evidence to support that high- versus low-mobility microglia represent distinct molecular phenotypes. Given that our time-lapse imaging spans only a three-hour window, it remains unclear whether these mobility states reflect stable cell-intrinsic properties or transient phases within a dynamic surveillance process. Notably, we observed that individual cells can transition between more stationary, neuron-associated states and highly mobile states within the same imaging session. In future work, we intend to investigate whether prolonged interactions with neuronal somas or other microenvironmental cues may drive diversification of reactive myeloid cell phenotypes.

(5) In the discussion, the authors speculate about "collective coordinated decision making" - that seems a stretch unless greater context is provided. The fact that several microglia can be found in contact with an individual neuron and that each microglia can connect with multiple neurons simultaneously is certainly interesting; however, evidence for hive behavior is entirely lacking.

We agree with the reviewer that our previous wording overstated the interpretation. The statement regarding collective decision-making has been removed.

Author response:

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

eLife Assessment:

This is an important study, supported by solid to convincing data, that suggests a model for diet selection in C. elegans. The significance is that while C. elegans has long been known to be attracted to bacterial volatiles, what specific bacterial volatiles may signify to C. elegans is largely unknown. This study also provides evidence for a possible odorant/GPCR pairing.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Siddiqui et al., investigate the question of how bacterial metabolism contributes to the attraction of C. elegans to specific bacteria. They show that C. elegans prefers three bacterial species when cultured in a leucine-enriched environment. These bacterial species release more isoamyl alcohol, a known C. elegans attractant, when cultured with leucine supplement than without leucine supplement. The study shows correlative evidence that isoamyl alcohol is produced from leucine by the Ehrlich pathway. In addition, they show that SRD-12 (SNIF-1) is likely a receptor for isoamyl alcohol because a null mutant of this receptor exhibits lower chemotaxis to isoamyl alcohol and lower preference for leucine-enriched bacteria.

Strengths:

(1) This study takes a creative approach to examine the question of what specific volatile chemicals released by bacteria may signify to C. elegans by examining both bacterial metabolism and C. elegans preference behavior. Although C. elegans has long been known to be attracted to bacterial metabolites, this study may be one of the first to examine the role of a specific bacterial metabolic pathway in mediating attraction.

(2)  A strength of the paper is the identification of SRD-12 (SNIF-1) as a likely receptor for isoamyl alcohol. The ligands for very few olfactory receptors have been identified in C. elegans and so this is a significant addition to the field. The srd-12 (snif-1) null mutant strain will likely be a useful reagent for many labs examining olfactory and foraging behaviors.

Weaknesses:

(1) The authors write that the leucine metabolism via the Ehrlich pathway is required for the production of isoamyl alcohol by three bacteria (CEent1, JUb66, BIGb0170), but their evidence for this is correlation and not causation. They write that the gene ilvE is a bacterial homolog of the first gene in the yeast Ehrlich pathway (it would be good to include a citation for this) and that the gene is present in these three bacterial strains. In addition, they show that this gene, ilvE, is upregulated in CEent1 bacteria upon exposure to leucine. To show causation, they need to knockout ilvE from one of these strains, show that the bacteria does not have increased isoamyl alcohol production when cultured on leucine, and that the bacteria is no longer attractive to C. elegans.

Thank you for the comment. We have added the appropriate citation [1,2]. We agree that worms’ diet preference for the preferred strains upon ilvE knockout will further strengthen the claim for IAA being used as a proxy for leucine-enriched diet. Currently, protocols and tools for genetic manipulations for CeMbio strains are not available, making this experiment not feasible at this time.  

(2) The authors examine three bacterial strains that C. elegans showed increased preference when grown with leucine supplementation vs. without leucine supplementation. However, there also appears to be a strong preference for another strain, JUb0393, when grown on plus leucine (Figure 1B). It would be good to include statistics and criteria for selecting the three strains.

Thanks for your comment. We agree that for Pantoea nemavictus, JUb393, worms seem to prefer the leucine supplemented (+ LEU) bacteria over unsupplemented (-LEU). However, when given a choice between the individual CeMbio bacteria and E. coli OP50, worms showed preference for only CEent1, JUb66, and BIGb0170 (Figure 1F). Consequently, CEent1, JUb66, and BIGb0170 were selected for further analyses. We have included statistics for Figure 1B-C and Figure S1A-G with details mentioned in the figure legend. 

(3) Although the behavioral evidence that srd-12 (snif-1) gene encodes a receptor for isoamyl alcohol is compelling, it does not meet the standard for showing that it is an olfactory receptor in C. elegans. To show it is indeed a likely receptor one or more of the following should be done:

(a) Calcium imaging of AWC neurons in response to isoamyl alcohol in the receptor mutant with the expectation that the response would be reduced or abolished in the mutant compared to wildtype.

(b)"A receptor swap" experiment where the SRD-12 (SNIF-1) receptor is expressed in AWB repulsive neuron in SRD-12 (SNIF-1) receptor mutant background with the expectation that with receptor swap C. elegans will now be repulsed from isoamyl alcohol in chemotaxis assays (experiment from Sengupta et al., 1996 odr-10 paper).

Thanks for all your comments and suggestions. While the lab currently does not have the necessary expertise to conduct calcium imaging of neurons, we have performed additional experiments to confirm the requirements of AWC neurons for SNIF-1 function. We generated transgenic worms with extrachromosomal array expressing snif-1 under (a) AWC-specific promoter, odr-1, and (b) AWB-specific promoter, str-1. As shown in new panel 6H in the revised manuscript and Author response image 1, we found that overexpression of snif-1 in AWC neurons completely rescues the chemotaxis defect of snif-1 mutant (referred at VSL2401), whereas upon the “receptor swap" in AWB neurons IAA is sensed as a repellent.  

Author response image 1.

(A) Chemotaxis index (CI) of WT, VSL2401, VSL2401 [AWCp::snif-1] and VSL2401 [AWBp::snif-1] worms to IAA at 1:1000 dilution. Significant differences are indicated as **** P ≤ 0.0001 determined by one-way ANOVA followed by post hoc Dunnett’s multiple comparison test. Error bars indicate SEM (n≥15).

(4) The authors conclude that C. elegans cannot detect leucine in chemotaxis assays. It is important to add the method for how leucine chemotaxis assay was done in order to interpret these results. Because leucine is not volatile if leucine is put on the plates immediately before the worms are added (as in a traditional odor chemotaxis assay), there is no leucine gradient for the worm to detect. It would be good to put leucine on the plate several hours before worms are introduced so worms have the possibility to be able to detect the gradient of leucine (for example, see Wakabayashi et al., 2009).

Previously, the chemotaxis assays with leucine were performed like traditional odor chemotaxis assays. We also performed chemotaxis assay as detailed in Shingai et al 2005[3]. Leucine was spotted on the assay plates 5 hours prior to the introduction of worms on the plates. As shown in new panel S1H in the revised manuscript, wild-type worms do not show response to leucine in the modified chemotaxis assay.

We have included the experimental details for leucine chemotaxis assays in the revised manuscript.  

(5) The bacterial preference assay entitled "odor-only assay" is a misleading name. In the assay, C. elegans is exposed to both volatile chemicals (odors) and non-volatile chemicals because the bacteria are grown on the assay plate for 12 hours before the worms are introduced to the assay plate. In that time, the bacteria is likely releasing non-volatile metabolites into the plate which may affect the worm's preference. A true odor-only assay would have the bacteria on the lid and the worms on the plate.

The ‘odor-only’ diet preference assay does not allow for non-volatile chemicals to reach worms. We achieved this by using tripartite dishes where the compartments containing worms and bacterial odors are separated by polystyrene barriers. At the time of the assay, worms were spotted in a separate compartment from that of bacteria (as shown in schematic 1A). The soluble metabolites released by the bacteria during their growth will accumulate in the agar within the bacterial compartment alone such that worms only encounter the volatile metabolites produced by bacteria wafting past the polystyrene barrier.

(6) The findings of the study should be discussed more in the context of prior literature. For example, AWC neurons have been previously shown to be involved in bacterial preference (Harris et al., 2014; Worthy et al., 2018). In addition, CeMbio bacterial strains (the strains examined in this study) have been previously shown to release isoamyl alcohol (Chai et al. 2024).

Thanks for the suggestion. We have modified the Discussion section to discuss the study in the light of relevant prior literature.  

Reviewer #2 (Public review):

Summary:

Siddiqui et al. show that C. elegans prefers certain bacterial strains that have been supplemented with the essential amino acid (EEA) leucine. They convincingly show that some leucine enriched bacteria stimulate the production of isoamyl alcohol (IAA). IAA is an attractive odorant that is sensed by the AWC. The authors an identify a receptor, SRD-12 (SNIF-1), that is expressed in the AWC chemosensory neurons and is required for chemotaxis to IAA. The authors propose that IAA is a predominant olfactory cue that determines diet preference in C. elegans. Since leucine is an EAA, the authors propose that worm IAA sensing allows the animal provides a proxy mechanism to identify EAA rich diets.

Strengths:

The authors propose IAA as a predominant olfactory cue that determines diet preference in C. elegans providing molecular mechanism underlying diet selection. They show that wild isolates of C. elegans have a strong chemotactic response to IAA indicating that IAA is an ecologically relevant odor for the worm. The paper is well written, and the presented data are convincing and well organized. This is an interesting paper that connects chemotactic response with bacterially produced odors and thus provides an understanding of how animals adapt their foraging behavior through the perception of molecules that may indicate the nutritional value.

Weaknesses:

Major:

While I do like the way the authors frame C. elegans IAA sensing as mechanisms to identify leucine (EAA) rich diets it is not fully clear whether bacterial IAA production is a proxy for bacterial leucine levels.

(1) Can the authors measure leucine (or other EAA) content of the different CeMbio strains? This would substantiate the premise in the way they frame this in the introduction. While the authors convincingly show that leucine supplementation induces IAA production in some strains, it is not clear if there are lower leucine levels in the different in non-preferred strains.

Thanks for your suggestion. Estimating leucine levels in various bacteria will provide useful information, and we hope to do so in future studies.

(2) It is not clear whether the non-preferred bacteria in Figure 1A and 1B have the ability to produce IAA. To substantiate the claim that C. elegans prefers CEent1, JUb66, and BIGb0170 due to their ability to generate IAA from leucine, it would measure IAA levels in non-preferred bacteria (+ and - leucine supplementation). If the authors have these data it would be good to include this.

Thanks for the suggestion. We have included the table indicating the presence or absence of IAA production by all the bacteria under + LEU and – LEU conditions (Table S2). Some of the nonpreferred bacteria indeed produce isoamyl alcohol. However, the abundance of IAA in these strains is significantly less than in the preferred bacteria.  

Using the available genomic sequence data, we found that all CeMbio strains encode IlvE-like transaminase enzymes[4]. This suggests that presumably all the bacteria have the metabolic capacity to make alpha-ketoisocaproate (an intermediate in IAA biosynthetic pathway) from leucine. However, the regulation of metabolic flux is likely to be quite complex in various bacteria.  

(3) The authors would strengthen their claim if they could show that deletion or silencing ilvE enzyme reduces IAA levels and eliminates the increased preference upon leucine supplementation.

We agree that testing worms’ diet preference for the preferred strains upon ilvE knockout will further strengthen the claim for IAA being crucial for finding leucine-enriched diet. Currently the lab does not have the necessary expertise and standardize protocols to do genetic manipulations for the CeMbio strains.

(4) While the three preferred bacteria possess the ilvE gene, it is not clear whether this enzyme is present in the other non-preferred bacterial strains. As far as I know, the CeMbio strains have been sequenced so it should be easy to determine if the non-preferred bacteria possess the capacity to make IAA. Does the expression of ilvE in e.g. E. coli increase its preference index or are the other genes in the biosynthesis pathway missing?

Thanks for the suggestion. Using the available genomic sequence data, we find that all the bacteria in the CeMbio collection possess IlvE-like transaminase necessary for synthesis of alphaketoisocaproate, key metabolite in leucine turn over as well as precursor for IAA [4]. E. coli has an IlvE encoding gene in its genome [2]. However, we do not find IAA in the headspace of E. coli either with or without leucine supplementation. This indicates either (i) E. coli lacks enzymes for subsequent steps in IAA biosynthesis or (ii) leucine provided under the experimental regime is not sufficient to shift the metabolic flux to IAA production.  

Previous studies have suggested that in yeast, the final two steps leading to IAA production are catalyzed by decarboxylase and dehydrogenase enzymes1. The genomic and metabolic flux data available for CeMbio do not describe specific enzymes leading up to IAA synthesis [4].  

(5) It is strongly implied that leucine-rich diets are beneficial to the worm. Do the authors have data to show the effect on leucine supplementation on C. elegans healthspan, life-span or broodsize?

Edwards et al. 2015 reported a 15% increase in the lifespan of worms upon 1 mM leucine supplementation [5]. Wang et al 2018 also showed lifespan extension upon 1 mM and 10 mM leucine supplementation. They also reported that while leucine supplementation did not have any effect on brood size, it did make worms more resistant to heat, paraquat, and UV-stress [6]. These studies have been included in the discussion section.

Other comments:

Page 6. Figure 2c. While the authors' conclusions are correct based on AWC expts. it would be good at this stage to include the possibility that odors that enriched in the absence of leucine may be aversive.

Thanks for the comment. We have tested the chemotaxis response of the worms for most of the odors produced by CeMbio strains without leucine supplementation. We did not find any odor that is aversive to worms. However, we cannot completely rule out the possibility that a low abundance of aversive odor in the headspace of the bacteria was missed.

Interestingly, we did identify 2-nonanone, a known repellent, in the headspace of the preferred bacteria upon leucine supplementation. However, the abundance of 2-nonanone in headspace of bacteria is relatively low (less than 1% for CEent1, and JUb66, and ~10% for BIGb0170). This suggests that the relative abundance of odors in an odor bouquet may be a relevant factor in determining worms’ reference.  

Page 6. IAA increases 1.2-4 folds upon leucine supplementation. If the authors perform a chemotaxis assay with just IAA with 1-2-4 fold differences do you get the shift in preference index as seen with the bacteria? i.e. is the difference in IAA concentration sufficient to explain the shift in bacterial PI upon leucine supplementation? Other attractants such as Acetoin and isobutanol go up in -Leu conditions.

Thanks for the suggestion. As shown in Figure S2H and S2I, when given a choice between a concentration of IAA (1:1000 dilution) attractive to worms and a 4-fold higher amount of IAA, worms chose the latter. This result suggests that worms can distinguish between relatively small difference in concentrations of IAA.

We agree that the relative abundance of Acetoin and Isobutanol is high in -LEU conditions. The presence of other attractants in - LEU conditions should skew the preference of worms for – LEU bacteria. However, we found that worms prefer + LEU bacteria (Figure 1B), suggesting that the abundance of IAA mainly influences the diet preference of the worms.  

Page 14-15. The authors identify a putative IAA receptor based on expression studies. I compliment the authors for isolating two CRISPR deletion alleles. They show that the srd-12 (snif-1) mutants have obvious defects in IAA chemotaxis. Very few ligand-odorant receptors combinations have been identified so this is an important discovery. CenGen data indicate that srd-12 (snif-1) is expressed in a limited set of neurons. Did the authors generate a reporter to show the expression of srd-12 (snif-1)? This is a simple experiment that would add to the characterization of the SRD-12 (SNIF-1) receptor. Rescue experiments would be nice even though the authors have independent alleles. To truly claim that SRD-12 (SNIF-1) is the ligand for IAA and activates the AWC neurons would require GCamp experiments in the AWC neuron or heterologous expression system. I understand that GCamp imaging might not be part of the regular arsenal of the lab but it would be a great addition (even in collaboration with one of the many labs that do this regularly). Comparing AWC activity using GCaMP in response IAA-producing bacteria with high leucine levels in both wild-type and SRD-12 (SNIF-1) deficient backgrounds, would further support their narrative. I leave that to the authors.

Thanks for your comments and suggestions. To address this comment, we rescued snif-1 mutant (referred as VSL2401) with extrachromosomal array expressing snif-1 under AWC-specific promoter as well as its native promoter. As shown in Figure 6H and Author response image 2, we find that both transgenic lines show a complete rescue of chemotaxis response to isoamyl alcohol. To find where snif-1 is expressed, we generated a transgenic line of worms expressing GFP under snif-1 promoter, and mCherry under odr-1 promoter (to mark AWC neurons). As shown in Figure 6I, we found that snif-1 is expressed faintly in many neurons, with strong expression in one of the two AWC neurons marked by odr-1::mCherry. This result suggests that SNIF-1 is expressed in AWC neuron.

We hope to perform GCaMP assay and further characterization of SNIF-1 in the future.

Author response image 2.

Chemotaxis index (CI) of WT, VSL2401, VSL2401 [AWCp:: snif-1] and VSL2401 [snif-1p::snif-1] worms to IAA at 1:1000 dilution. Significant differences are indicated as **** P ≤ 0.0001 determined by one-way ANOVA followed by post hoc Dunnett’s multiple comparison test. Error bars indicate SEM (n≥15).

Minor:

Page 4 "These results suggested that worms can forage for diets enriched in specific EAA, leucine...." More precise at this stage would be to state " These results indicated that worms can forage for diets supplemented with specific EAA...".

We have changed the statement in the revised manuscript.

Page 5."these findings suggested that worms not only rely on odors to choose between two bacteria but also to find leucine enriched bacteria" This statement is not clear to me and doesn't follow the data in Fig. S2. Preferred diets in odorant assays are the IAA producing strains.

Thanks for your comment. We have revised the manuscript to make it clear. “Altogether, these findings suggested that worms rely on odors to distinguish different bacteria and find leucineenriched bacteria”. This statement concludes all the data shown in Figure 1 and Figure S1.  

Page 5. Figure S2A provides nice and useful data that can be part of the main Figure 1.

Thanks for the comment. We have incorporated the data from Figure S2A to main Figure 1.

Reviewer #3 (Public review):

Summary:

The authors first tested whether EAA supplementation increases olfactory preference for bacterial food for a variety of bacterial strains. Of the EAAs, they found only leucine supplementation increased olfactory preference (within a bacterial strain), and only for 3 of the bacterial strains tested. Leucine itself was not found to be intrinsically attractive.

They determined that leucine supplementation increases isoamyl alcohol (IAA) production in the 3 preferred bacterial strains. They identify the biochemical pathway that catabolizes leucine to IAA, showing that a required enzyme for this pathway is upregulated upon supplementation.

Consistent with earlier studies, they find that AWC olfactory neuron is primarily responsible for increased preference for IAA-producing bacteria.

Testing volatile compounds produced by bacteria and identified by GC/MS, and identified several as attractive, most of them require AWC for the full effect. Adaptation assays were used to show that odorant levels produced by bacterial lawns were sufficient to induce olfactory adaptation, and adaptation to IAA reduced chemotaxis to leucine-supplemented lawns. They then showed that IAA attractiveness is conserved across wild strains, while other compounds are more variable, suggesting IAA is a principal foraging cue.

Finally, using the CeNGEN database, they developed a list of candidate IAA receptors. Using behavioral tests, they show that mutation of srd-12 (snif-1) greatly impairs IAA chemotaxis without affecting locomotion or attraction to another AWC-sensed odor, PEA.

Comments

This study will be of great interest in the field of C. elegans behavior, chemical senses and chemical ecology, and understanding of the sensory biology of foraging.

Strengths:

The identification of a receptor for IAA is an excellent finding. The combination of microbial metabolic chemistry and the use of natural bacteria and nematode strains makes an extremely compelling case for the ecological and adaptive relevance of the findings.

Weaknesses:

AWC receives synaptic input from other chemosensory neurons, and thus could potentially mediate navigation behaviors to compounds detected in whole or in part by those neurons. Language concluding detection by AWC should be moderated (e.g. p9 "worms sense an extensive repertoire...predominantly using AWC") unless it has been demonstrated.

Thanks for your comment. We have modified the manuscript to incorporate the suggestion.

srd-12 (snif-1) is not exclusively expressed in AWC. Normally, cell-specific rescue or knockdown would be used to demonstrate function in a specific cell. The authors should provide such a demonstration or explain why they are confident srd-12 (snif-1) acts in AWC.

Thanks for the comment. We have performed AWC-specific rescue of snif-1 in mutant worms. As shown in Figure 6H, we found that AWC neurons specific rescue completely recovered the chemotaxis defect of the snif-1 mutant (referred as VSL2401) for IAA. In addition, snif-1 is expressed in one of the AWC neurons.

A comparison of AWC's physiological responses between WT and srd-12 (snif-1), preferably in an unc13 background, would be nice. Even further, the expression of srd-12 (snif-1) in a different neuron type and showing that it confers responsiveness to IAA (in this case, inhibition) would be very convincing.

Thanks for the suggestion. We have performed a receptor swap experiment, where snif-1 is misexpressed in AWB neurons. We find that these worms show slight but significant repulsion to IAA compared to WT and snif-1 mutant worms (Author response image 1).

Recommendations for the authors:

Reviewing Editor:

Please consider all of the reviewer comments. In particular, as noted in the individual reviews, the strength of the evidence would be bolstered by additional experiments to demonstrate that the iLvE enzyme affects IAA levels in the preferred bacteria. The reviewers note that the authors haven't shown that IAA production is a reflection of leucine content. Are the non-preferred bacteria low on leucine or lack iLvE or IAA synthesis pathways? Further, more direct evidence that SRD-12 (SNIF-1) is in fact the primary IAA receptor would further strengthen the study. The authors should also be aware that geographic distance for wild isolate C. elegans may not directly correlate with phylogenetic distance. This should be assessed/discussed for the strains used.

Thanks for the suggestions. Some of these have been addressed in response to reviewers. Thanks for your comments about possible disconnect between geographical and phylogenetic distances amongst natural isolates used here.

By analyzing the phylogenetic tree generated using neighbor-joining algorithm available at CaeNDR database, we found that QX1211 and JU3226 are phylogenetically close, but the remaining isolates fall under different clades separated by long phylogenetic distances [7,8].  

Reviewer #1 (Recommendations for the authors):

(1) In the first sentence of the third paragraph of the introduction, C. elegans are described as "soildwelling." Although C. elegans has been described as soil-dwelling in the past, current research indicates they are most often found on rotten fruit, compost heaps and other bacterial-rich environments, not soil. "All Caenorhabditis species are colonizers of nutrient- and bacteria-rich substrates and none of them is a true soil nematode." from Kiontke, K. and Sudhaus, W. Ecology of Caenorhabditis species (WormBook).

Your specific comment about C. elegans’ habitat is well received. However, in that sentence we are referring to the chemosensory system of soil-dwelling animals in general, and not particularly C. elegans.

(2) Figure 3K, the model would be clearer if leucine-rich diet -> volatile chemicals ->AWC (instead of leucine-rich diet -> AWC <- volatile chemicals). The leucine-rich diet results in the production of volatile chemicals which are detected by AWC.

We have modified the figure to make it clearer.

(3) Figure 4 - it would help to include a table summarizing the volatile chemicals that each bacteria releases. Then the reader could more easily evaluate whether the adaptation to each specific odor is consistent with the change in preference for the specific bacteria based on what it releases in its headspace. In addition, Figure 4 would help to clarify whether bacteria in these experiments were cultured with or without leucine supplementation.

Table S2 summarizes the odors released by all the bacteria under + LEU and – LEU conditions.

In Figure 4, adaptation was performed by odors of bacteria when cultured under leucineunsupplemented conditions.

Reviewer #2 (Recommendations for the authors):

Page 9. Previous studies e.g. Bargmann Hartwieg and Horvitz have shown IAA is sensed by the AWC. Would be good to cite appropriately.

Thanks for the comment. The reference has been cited at p9 and p16.

References:

(1) Yuan, J., Mishra, P., and Ching, C.B. (2017). Engineering the leucine biosynthetic pathway for isoamyl alcohol overproduction in Saccharomyces cerevisiae. Journal of Industrial Microbiology and Biotechnology 44, 107-117. 10.1007/s10295-016-1855-2 %J Journal of Industrial Microbiology and Biotechnology.

(2) Kanehisa, M., Furumichi, M., Sato, Y., Matsuura, Y., and Ishiguro-Watanabe, M. (2025). KEGG: biological systems database as a model of the real world. Nucleic Acids Res 53, D672-d677. 10.1093/nar/gkae909.

(3) Shingai, R., Wakabayashi, T., Sakata, K., and Matsuura, T. (2005). Chemotaxis of Caenorhabditis elegans during simultaneous presentation of two water-soluble attractants, llysine and chloride ions. Comparative biochemistry and physiology. Part A, Molecular & integrative physiology 142, 308-317. 10.1016/j.cbpa.2005.07.010.

(4) Dirksen, P., Assié, A., Zimmermann, J., Zhang, F., Tietje, A.M., Marsh, S.A., Félix, M.A., Shapira, M., Kaleta, C., Schulenburg, H., and Samuel, B.S. (2020). CeMbio - The Caenorhabditis elegans Microbiome Resource. G3 (Bethesda, Md.) 10, 3025-3039. 10.1534/g3.120.401309.

(5) Edwards, C., Canfield, J., Copes, N., Brito, A., Rehan, M., Lipps, D., Brunquell, J., Westerheide, S.D., and Bradshaw, P.C. (2015). Mechanisms of amino acid-mediated lifespan extension in Caenorhabditis elegans. BMC genetics 16, 8. 10.1186/s12863-015-0167-2.

(6) Wang, H., Wang, J., Zhang, Z.J.J.o.F., and Research, N. (2018). Leucine Exerts Lifespan Extension and Improvement in Three Types of Stress Resistance (Thermotolerance, AntiOxidation and Anti-UV Irradiation) in C. elegans. 6, 665-673.

(7) Crombie, T.A., McKeown, R., Moya, N.D., Evans, Kathryn S., Widmayer, Samuel J., LaGrassa, V., Roman, N., Tursunova, O., Zhang, G., Gibson, Sophia B., et al. (2023). CaeNDR, the Caenorhabditis Natural Diversity Resource. Nucleic Acids Research 52, D850-D858. 10.1093/nar/gkad887 %J Nucleic Acids Research.

(8) Cook, D.E., Zdraljevic, S., Roberts, J.P., and Andersen, E.C. (2017). CeNDR, the Caenorhabditis elegans natural diversity resource. Nucleic Acids Res 45, D650-d657. 10.1093/nar/gkw893.

Author response:

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

Public Reviews: 

Reviewer #1 (Public review): 

Summary: 

This work by Al-Jezani et al. focused on characterizing clonally derived MSC populations from the synovium of normal and osteoarthritis (OA) patients. This included characterizing the cell surface marker expression in situ (at time of isolation), as well as after in vitro expansion. The group also tried to correlate marker expression with trilineage differential potential. They also tested the ability of the different subpopulations for their efficacy in repairing cartilage in a rat model of OA. The main finding of the study is that CD47hi MSCs may have a greater capacity to repair cartilage than CD47lo MSCs, suggesting that CD47 may be a novel marker of human MSCs that have enhanced chondrogenic potential. 

Strengths: 

Studies on cell characterization of the different clonal populations isolated indicate that the MSC are heterogenous and traditional cell surface markers for MSCs do not accurately predict the differentiation potential of MSCs. While this has been previously established in the field of MSC therapy, the authors did attempt to characterize clones derived from single cells, as well as evaluate the marker profile at the time of isolation. While the outcome of heterogeneity is not surprising, the methods used to isolate and characterize the cells were well developed. The interesting finding of the study is the identification of CD47 as a potential MSC marker that could be related to chondrogenic potential. The authors suggest that MSCs with high CD47 repaired cartilage more effectively than MSC with low CD47 in a rat OA model. 

Weaknesses: 

While the identification of CD47 as a novel MSC marker could be important to the field of cell therapy and cartilage regeneration, there was a lack of robust data to support the correlation of CD47 expression to chondrogenesis. The authors indicated that the proteomics suggested that the MSC subtype expressed significantly more CD47 than the non-MSC subtype. However, it was difficult to appreciate where this was shown. It would be helpful to clearly identify where in the figure this is shown, especially since it is the key result of the study. The authors were able to isolate CD47hi and CD47 low cells. While this is exciting, it was unclear how many cells could be isolated and whether they needed to be expanded before being used in vivo. Additional details for the CD47 studies would have strengthened the paper. Furthermore, the CD47hi cells were not thoroughly characterized in vitro, particularly for in vitro chondrogenesis. More importantly, the in vivo study where the CD47hi and CD47lo MSCs were injected into a rat model of OA lacked experimental details regarding how many cells were injected and how they were labeled. No representative histology was presented and there did not seem to be a statistically significant difference between the OARSI score of the saline injected and MSC injected groups. The repair tissue was stained for Sox9 expression, which is an important marker of chondrogenesis but does not show production of cartilage. Expression of Collagen Type II would be needed to more robustly claim that CD47 is a marker of MSCs with enhanced repair potential. 

Reviewer #2 (Public review): 

Summary: 

This is a compelling study that systematically characterized and identified clonal MSC populations derived from normal and osteoarthritis human synovium. There is immense growth in the focus on synovial-derived progenitors in the context of both disease mechanisms and potential treatment approaches, and the authors sought to understand the regenerative potential of synovial-derived MSCs. 

Strengths: 

This study has multiple strengths. MSC cultures were established from an impressive number of human subjects, and rigorous cell surface protein analyses were conducted, at both pre-culture and post-culture timepoints. In vivo experiments using a rat DMM model showed beneficial therapeutic effects of MSCs vs non-MSCs, with compelling data demonstrating that only "real" MSC clones incorporate into cartilage repair tissue and express Prg4. Proteomics analysis was performed to characterize non-MSC vs MSC cultures, and high CD47 expression was identified as a marker for MSC. Injection of CD47-Hi vs CD47-Low cells in the same rat DMM model also demonstrated beneficial effects, albeit only based on histology. A major strength of these studies is the direct translational opportunity for novel MSC-based therapeutic interventions, with high potential for a "personalized medicine" approach. 

Weaknesses: 

Weaknesses of this study include the rather cursory assessment of the OA phenotype in the rat model, confined entirely to histology (i.e. no microCT, no pain/behavioral assessments, no molecular readouts). It is somewhat unclear how the authors converged on CD47 vs the other factors identified in the proteomics screen, and additional information is needed to understand whether true MSCs only engraft in articular cartilage or also in ectopic cartilage (in the context of osteophyte/chondrophyte formation). Some additional discussion and potential follow-up analyses focused on other cell surface markers recently described to identify synovial progenitors is also warranted. A conceptual weakness is the lack of discussion or consideration of the multiple recent studies demonstrating that DPP4+ PI16+ CD34+ stromal cells (i.e. the "universal fibroblasts") act as progenitors in all mesenchymal tissues, and their involvement in the joint is actively being investigated. Thus, it seems important to understand how the MSCs of the present study are related to these DPP4+ progenitors. Despite these areas for improvement, this is a strong paper with a high degree of rigor, and the results are compelling, timely, and important. 

Overall, the authors achieved their aims, and the results support not just the therapeutic value of clonally-isolated synovial MSCs but also the immense heterogeneity in stromal cell populations (containing true MSCs and non-MSCs) that must be investigated further. Of note, the authors employed the ISCT criteria to characterize MSCs, with mixed results in pre-culture and post-culture assessments. This work is likely to have a longterm impact on methodologies used to culture and study MSCs, in addition to advancing the field's knowledge about how synovial-derived progenitors contribute to cartilage repair in vivo.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

In all figures, it would be beneficial to report the sample number used for the data reported. It is difficult to appreciate the statistical analysis without that information.

Understood, the sample number and replicates have been added to each figure legend.

Please check that Table S7 is part of the manuscript. It could not be found.

It was added as an additional excel file since it was too large to fit in the word document.

Lines 377-379 (Figure 2E): the authors write that rats receiving MSCs had a significantly lower OARSI and Krenn score vs. rats injected with non-MSCs. However, none of the bars indicating statistical significance run between these two groups. Please verify the text and figure.

This has been corrected

The details surrounding the labeling of the cells with tdTomato were not presented in the methods. 

This has been added to the methods

The fluorescent antibodies used should be listed and more details provided in the methods rather than a general statement that fluorescent antibodies were used.

Our apologies, the clones and companies have been added.

Additional information on the CD47 experiments (# cells, # animals) would have strengthened the study.

This has been added to the methods and figure legend.

Reviewer #2 (Recommendations for the authors): 

My comments span minor corrections, requests for additional analyses, some suggestions for additional experiments, and requests for additional discussion of recent important studies. 

Introduction: 

The introduction is thorough and well-written. I recommend a brief discussion about the emerging evidence demonstrating that DPP4+ PI16+ CD34+ synovial cells, i.e. the "universal fibroblasts", act as stromal progenitors in development, homeostasis, and disease. Relevant osteoarthritis-related papers encompass human and mouse studies (PMIDs: 39375009, 38266107, 38477740, 36175067, 36414376).

This has been added.

Relatedly, as DPP4 is CD26 and therefore useful as a cell-surface antigen for flow cytometry, sorting, etc, it would be interesting to understand the relationship and similarities between the CD47-High cells identified in this study and the DPP4/PI16+ cells previously described. Do they overlap in phenotype/identity?

We have added a new flow cytometry figure for address this question. 

Results: 

Note type-o on Line 311: "preformed" instead of "performed". Line 313 "prolife" instead of "profile"

Thank you for catching these.

The identified convergence of the cell surface marker profile of all normal and OA clones in culture is a highly intriguing result. Do the authors have stored aliquots of these cells to demonstrate whether this would also occur in soft substrate, i.e. low stiffness culture conditions? This could be done with standard dishes coated with bulk collagen or with commercially available low-stiffness dishes (1 kPa). This is relevant to multiple studies demonstrating the induction of a myofibroblast-like phenotype by stromal cells cultured on high-stiffness plastic or glass. This is also the experiment where assessment of DPP4/CD26 could be added, if possible.

While we agree it would be interesting to determine the mechanism by which the cells phenotypes converge, we would argue that it is outside of the scope of the current manuscript. We have instead added a sentence to the discussion. 

Line 353 regarding the use of CD68 as a negative gate: can the authors pleasecomment on why they employed CD68 here and not CD45? While monocytes/macs/myeloid cells are the most abundant immune cells in synovium, CD45 would more comprehensively exclude all immune cells. 

That is a fair point, and we really don’t have any reason to have picked CD68 over CD45. In our opinion either would be a fair negative marker to use based on the literature. 

Fig 2, minor suggestion: consider adding "MSC vs non-MSC" on the experimental schematic to more comprehensively summarize the experiment. 

This has been modified 

Fig 2E should show all individual datapoints, not just bar graphs. 

This has been modified

Fig 2: Given the significant reduction in Krenn score in DMM-MSC injected knees compared to DMM-saline knees, Fig 2 should also show representative images of the synovial phenotype to demonstrate which aspects of synovial pathology were mitigated. Was the effect related to lining hyperplasia, subsynovial infiltrate, fibrosis, etc? Similarly, can the authors narrate which aspects of the OARSI score drove the treatment effect (proteoglycans vs structure vs osteophytes, etc). 

We have added a new sup figure breaking down the Krenn score as well as higher magnification images of representative synovium.

Fig 2: In the absence of microCT imaging, can the authors quantify subchondral bone morphometrics using multiple histological sections? The tibial subchondral bone in Fig 2D appears protected from sclerosis/thickening.

Unfortunately, this is beyond what are able to add to the manuscript. 

The Fig 3 results are highly compelling and interesting. Congratulations.

Thank you very much.

Fig 4A: the cell highlighted in the high-mag zoom box in Fig 4A appears to be localized within the joint capsule or patellar tendon (it is unclear which anatomic region this image represents). The highly aligned nature of the tissue and cells along a fibrillar geometry indicates that this is not synovium. The interface between synovium and the tissue in question can be clearly observed in this image. Please choose an image more representative of synovium.

We completely agree with the reviewers assessment. However, it is the synovium that overlays this tissue (Fig 4A arrow). We are simply showing that there were very few MSCs that took up residence in the synovium or the adjacent tissues. 

Fig 4C and F: please show individual data points.

This has been added

Fig 5D: I see DPP4 and ITGA5 were also hits in the proteomics analysis, which is intriguing. Besides my comments/suggestions regarding DPP4 above, please note this recent paper identifying a ITGA5+ synovial fibroblast subset that orchestrates pathological crosstalk with lymphocytes in RA, PMID: 39486872

Thank you for the information. We have added the reference in the results section. 

Fig 5B-D: How did the authors converge on CD47 as the target for follow-up study? It does not appear to be a differentially-expressed protein based on the Volcano plot in Fig 5B, and it's unclear why it is a more important factor than any of the other proteins shown in the network diagram in Fig 5D, e.g. CTSL, ITGA5, DPP4. Can the authors add a quantitative plot supporting their statement "the MSC sub-type expressed significantly more CD47 than the non-MSCs" on Line 458? 

We have re-written this line. It was incorrect to discuss amount of CD47. That was shown later with the flow analysis.  

Fig 6D: Please show individual data points and also representative histology images to demonstrate the nature of the phenotypic effect.

This has been added. 

Fig 6E-F: In what anatomic region are these images? Please add anatomic markers to clarify the location and allow the reader to interpret whether this is articular cartilage or ectopic cartilage

We have redone the figure to show the area as requested.

Relevant to this, do the authors observe this type of cellular engraftment in ectopic cartilage/osteophytes or only in articular cartilage? Understanding the contribution of these cells to the formation/remodeling of various cartilage types in the context of OA is a critical aspect of this line of investigation.

We didn’t see any contribution of these cells to ectopic cartilage formation and are actively working on a follow up study discussing this point specifically. 

Discussion: 

Besides my comments regarding DPP4 and ITGA5 above, the authors may also consider discussing PMID: 37681409 (JCI Insight 2023), which demonstrates that adult Prg4+ progenitors derived from synovium contribute to articular cartilage repair in vivo. 

We agree that there are numerous markers we could look at in future studies and that other people in the field are actively studying.

Author response:

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary:

The manuscript submitted by Langenbacher et al., entitled " Rtf1-dependent transcriptional pausing regulates cardiogenesis", describes very interesting and highly impactful observations about the function of Rtf-1 in cardiac development. Over the last few years, the Chen lab has published novel insights into the genes involved in cardiac morphogenesis. Here, they used the mouse model, the zebrafish model, cellular assays, single cell transcription, chemical inhibition, and pathway analysis to provide a comprehensive view of Rtf1 in RNAPII (Pol2) transcription pausing during cardiac development. They also conducted knockdown-rescue experiments to dissect the functions of Rtf1 domains. 

Strengths:

The most interesting discovery is the connection between Rtf1 and CDK9 in regulating Pol2 pausing as an essential step in normal heart development. The design and execution of these experiments also demonstrate a thorough approach to revealing a previously underappreciated role of Pol2 transcription pausing in cardiac development. This study also highlights the potential amelioration of related cardiac deficiencies using small molecule inhibitors against cyclin dependent kinases, many of which are already clinically approved, while many other specific inhibitors are at various preclinical stages of development for the treatment of other human diseases. Thus, this work is impactful and highly significant. 

We thank the reviewer for appreciating our work.

Reviewer #2 (Public Review): 

Summary: 

Langenbacher at el. examine the requirement of Rtf1, a component of the PAF1C, which regulates transcriptional pausing in cardiac development. The authors first confirm their previous morphant study with newly generated rtf1 mutant alleles, which recapitulate the defects in cardiac progenitor and diUerentiation gene expression observed previously in morphants. They then examine the conservation of Rtf1 in mouse embryos and embryonic stem cell-derived cardiomyocytes. Conditional loss of Rtf1 in mesodermal lineages and depletion in murine ESCs demonstrates a failure to turn on cardiac progenitor and diUerentiation marker genes, supporting conservation of Rtf1 in promoting cardiac development. The authors subsequently employ bulk RNA-seq on flow-sorted hand2:GFP+ cells and multiomic single-cell RNA-seq on whole Rtf1-depleted embryos at the 10-12 stage. These experiments corroborate that genes associated with cardiac and muscle development are lost. Furthermore, the diUerentiation trajectories suggest that the expression of genes associated with cardiac maturation is not initiated.  Structure-function analysis supports that the Plus3 domain is necessary for its function in promoting cardiac progenitor formation. ChIP-seq for RNA Pol II on 1012 somite stage embryos suggests that Rtf1 is required for proper promoter pausing. This defect can partially be rescued through use of a pharmacological inhibitor for Cdk9, which inhibits elongation, can partially restore elongation in rtf1 mutants.  

Strengths: 

Many aspects of the data are strong, which support the basic conclusions of the authors that Rtf1 is required for transcriptional pausing and has a conserved requirement in vertebrate cardiac development. Areas of strength include the genetic data supporting the conserved requirement for Rtf1 in promoting cardiac development, the complementary bulk and single-cell RNA-sequencing approaches providing some insight into the gene expression changes of the cardiac progenitors, the structure-function analysis supporting the requirement of the Plus3 domain, and the pharmacological epistasis combined with the RNA Pol II ChIP-seq, supporting the mechanism implicating Cdk9 in the Rtf1 dependent mechanism of RNA Pol II pausing. 

We thank the reviewer for the summary and for recognizing many strengths of our work. 

Weaknesses: 

While most of the basic conclusions are supported by the data, there are a number of analyses that are confusing as to why they chose to perform the experiments the way they did and some places where the interpretations presently do not support the interpretations. One of the conclusions is that the phenotype aUects the maturation of the cardiomyocytes and they are arresting in an immature state. However, this seems to be mostly derived from picking a few candidates from the single cell data in Fig. 6. If that were the case, wouldn't the expectation be to observe relatively normal expression of earlier marker genes required for specification, such as Nkx2.5 and Gata5/6? The in situ expression analysis from fish and mice (Fig. 2 and Fig. 3) and bulk RNA-seq (Fig. 5) seems to suggest that there are pretty early specification and diUerentiation defects. While some genes associated with cardiac development are not changed, many of these are not specific to cardiomyocyte progenitors and expressed broadly throughout the ALPM. Similarly, it is not clear why a consistent set of cardiac progenitor genes (for instance mef2ca, nkx2.5, and tbx20) was analyzed for all the experiments, in particular with the single cell analysis. 

A major conclusion of our study is that Rtf1 deficiency impairs myocardial lineage differentiation from mesoderm, as suggested by the reviewer. Thus, the main goal of this study is to understand how Rtf1 drives cardiac differentiation from the LPM, rather than the maturation of cardiomyocytes.  Multiple lines of evidence support this conclusion:

(a) In situ hybridization showed that Rtf1 mutant embryos do not have nkx2.5+ cardiac progenitor cells and subsequently fail to produce cardiomyocytes (Figs. 2, 3).

(b) RT-PCR analysis showed that knockdown of Rtf1 in mouse embryonic stem cells causes a dramatic reduction of cardiac gene expression and production of significantly fewer beating patches (Fig.4).

(c) Bulk RNA sequencing revealed significant downregulation of cardiac lineage genes, including nkx2.5 (Fig. 5).

(d) Single cell RNA sequencing clearly showed that lateral plate mesoderm (LPM) cells are significantly more abundant in Rtf1 morphant,s whereas cardiac progenitors are less abundant (Fig. 6 and Fig.6 Supplement 1-5). 

When feasible, we used cardiac lineage restricted markers in our assays. Nkx2.5 and tbx5a are not highlighted in the single cell analysis because their expression in our sc-seq dataset was too low to examine in the clustering/trajectory analysis.  In this revised manuscript, we provide violin plots showing the low expression levels of these genes in single cells from Rtf1 deficient embryos (Figure 6 Supplement 5).

The point of the multiomic analysis is confusing. RNA- and ATAC-seq were apparently done at the same time. Yet, the focus of the analysis that is presented is on a small part of the RNA-seq data. This data set could have been more thoroughly analyzed, particularly in light of how chromatin changes may be associated with the transcriptional pausing. This seems to be a lost opportunity. Additionally, how the single cell data is covered in Supplemental Fig. 2 and 3 is confusing. There is no indication of what the diUerent clusters are in the Figure or the legend. 

In this study, we performed single cell multiome analysis and used both scRNAseq and scATACseq datasets to generate reliable clustering.  The scRNAseq analysis reveals how Rtf1 deficiency impacts cardiac differentiation from mesoderm, which inspired us to investigate the underlying mechanism and led to the discovery of defects in Rtf1-dependent transcriptional pause release.

We agree with the reviewer that deep examination of Rtf1-dependent chromatin changes would provide additional insights into how Rtf1 influences early development and careful examination of the scATACseq dataset is certainly a good future direction.  

In this revised manuscript, we have revised Fig.6 Supplement 1 to include the predicted cell types and provide an additional excel file showing the annotation of all 39 clusters (Supplementary Table 2). 

While the effect of Rtf1 loss on cardiomyocyte markers is certainly dramatic, it is not clear how well the mutant fish have been analyzed and how specific the eUect is to this population. It is interpreted that the eUects on cardiomyocytes are not due to "transfating" of other cell fates, yet supplemental Fig. 4 shows numerous eUects on potentially adjacent cell populations. Minimally, additional data needs to be provided showing the live fish at these stages and marker analysis to support these statements. In some images, it is not clear the embryos are the same stage (one can see pigmentation in the eyes of controls that is not in the mutants/morphants), causing some concern about developmental delay in the mutants. 

Single cell RNA sequencing showed an increased abundance of LPM cells and a reduced abundance of cardiac progenitors in Rtf1 morphants (Fig. 6 and Fig.6 Supplement 1-5). The reclustering of anterior lateral plate mesoderm (ALPM) cells and their derivatives further showed that cells representing undiRerentiated ALPM were increased whereas cells representing all three ALPM derivatives were reduced. These findings indicate a defect in ALPM diRerentiation. 

The reviewer questioned whether we examined stage-matched embryos. In our assay, Rtf1 mutant embryos were collected from crosses of Rtf1 heterozygotes. Each clutch from these crosses consists of ¼ embryos showing rtf1 mutant phenotypes and ¾ embryos showing wild type phenotypes which were used as control. Mutants and their wild type siblings were fixed or analyzed at the same time.

The reviewer questioned the specificity of the Rtf1 deficient cardiac phenotype and pointed out that Rtf1 mutant embryos do not have pigment cells around the eye.  Rtf1 is a ubiquitously expressed transcriptional regulator.  Previous studies in zebrafish have shown that Rtf1 deficiency significantly impacts embryonic development. Rtf1 deficiency causes severe defects in cardiac lineage and neural crest cell development; consequently, Rtf1 deficient embryos do not have cardiomyocytes and pigmentation (Langenbacher et al., 2011, Akanuma et al., 2007, and Jurynec et al., 2019).  We now provide an image showing a 2-day-old Rtf1 mutant embryo and their wild type sibling to illustrate the cardiac, neural crest, and somitogenesis defects caused by loss of Rtf1 activity (Fig. 2 Supplement 1).

With respect to the transcriptional pausing defects in the Rtf1 deficient embryos, it is not clear from the data how this eUect relates to the expression of the cardiac markers. This could have been directly analyzed with some additional sequencing, such as PRO-seq, which would provide a direct analysis of transcriptional elongation. 

We showed that Rtf1 deficiency results in a nearly genome-wide decrease in promoterproximal pausing and downregulation of cardiac makers. Attenuating transcriptional pause release could restore cardiomyocyte formation in Rtf1 deficient embryos. In this revised manuscript, we provide additional RNAseq data showing that the expression levels of critical cardiac development genes such as nkx2.5, tbx5a, tbx20, mef2ca, mef2cb, ttn.2, and ryr2b are significantly rescued.  We agree with the reviewer that further analyses using the PRO-seq approach could provide additional insights, but it is beyond the scope of this manuscript. 

Some additional minor issues include the rationale that sequence conservation suggests an important requirement of a gene (line 137), which there are many examples this isn't the case, referencing figures panels out of order in Figs. 4, 7, and 8) as described in the text, and using the morphants for some experiments, such as the rescue, that could have been done in a blinded manner with the mutants. 

We have clarified the rationale in this revised manuscript and made the eRort to reference figures in order. 

The reviewer commented that rescue experiments “could have been done in a blinded manner with the mutants”. This was indeed how the flavopiridol rescue and cdk9 knockdown experiments were carried out. Embryos from crosses of Rtf1 heterozygotes were collected, fixed after treatment and subjected to in situ hybridization. Embryos were then scored for cardiac phenotype and genotyped (Fig.8 d-g). Morpholino knockdown was used in genomic experiments because our characterization of rtf1 morphants showed that they faithfully recapitulate the rtf1 mutant phenotype during the timeframe of interest (Fig. 2).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

This reviewer has a few suggestions below, aimed at improving the clarity and impact of the current study. Once these items are addressed, the manuscript should be of interest to the Elife reader. 

Item 1. Strengthening the interaction between Rfh1 and CDK9 on Pol2 pausing. 

The authors have convincingly shown that the chemical inhibition of CDK9 by flavopiridol can partially rescue the expression of cardiac genes in the zebrafish model. Although flavopiridol is FDA approved and has been a classical inhibitor for the dissection of CDK9 function, it also inhibits related CDKs (such as Flavopiridol (Alvocidib) competes with ATP to inhibit CDKs including CDK1, CDK2, CDK4, CDK6, and CDK9 with IC50 values in the 20-100 nM range) Therefore, this study could be more impactful if the authors can provide evidence on which of these CDKs may be most relevant during Rtf1-dependent cardiogenesis. To determine whether the observed cardiac defect indicates a preferential role for CDK9, or that other CDKs may also be able to provide partial rescue may be clarified using additional, more selective small molecules (e.g., BAY1251152, LDC000067 are commercially available). 

The reviewer raised a reasonable concern about the specificity of flavopiridol. We thank the reviewer for the insightful suggestion and share the concern about specificity. To address this question, we have used an orthogonal testing through morpholino inhibition where we directly targeted CDK9 and observed the same level of rescue, supporting a critical role of transcription pausing in cardiogenesis.

Item 2. Differences between CRISPR lines and morphants 

Much of the work presented used Rtf1 morphants while the authors have already generated 2 CRISPR lines. What is the diUerence between morphants and mutants? The authors should comment on the similarities and/or differences between using morphants or mutants in their study and whether the same Rtf1- CDK9 connection also occurs in the CRISPR lines. 

The morphology of our mutants (rtf1^LA2678 and rtf1^LA2679) resembles the morphants and the previously reported ENU-induced rtf1^KT641 allele. Extensive in situ hybridization analysis showed that the morphants faithfully recapitulate the mutant phenotypes (Fig.2). We have performed rescue experiments (flavopiridol and CDK9 morpholino) using Rtf1 mutant embryos and found that inhibiting Cdk9 restores cardiomyocyte formation (Fig.8). 

Item 3. Discuss the therapeutic relevance of study 

The authors have already generated a mouse model of Rtf1 Mesp1-Cre knockout where cardiac muscle development is severely derailed (Fig 3B). Thus, a demonstration of a conserved role for CDK9 inhibitor in rescuing cardiogenesis using mouse cells or the mouse model will provide important information on a conserved pathway function relevant to mammalian heart development. In the Discussion, how this underlying mechanistic role may be useful in the treatment of congenital heart disease should be provided.  

Thank you for the insight. We have incorporated your comments in the discussion. 

Item 4. Insights into the role of CDK9-Rtf1 in response to stress versus in cardiogenesis. 

In the Discussion, the authors commented on the role of additional stress-related stimuli such as heat shock and inflammation that have been linked to CDK9 activity. However, the current ms provides the first, endogenous role of Pol2 pausing in a critical developmental step during normal cardiogenesis. The authors should emphasize the novelty and significance of their work by providing a paragraph on the state of knowledge on the molecular mechanisms governing cardiogenesis, then placing their discovery within this framework. This minor addition will also clarify the significance of this work to the broad readership of eLife. 

Thank you for the suggestion. We have incorporated your comments and elaborate on the novelty and significance of our work in the discussion. 

Reviewer #2 (Recommendations For The Authors): 

(1) It is diUicult to assess what the overt defects are in the embryos at any stages. Images of live images were not included in the supplement. Do these have a small, malformed heart tube later or are the embryos just deteriorating due to broad defects? 

The Rtf1 deficient embryos do not produce nkx2.5+ cardiac progenitors. Consequently, we never observed a heart tube or detected cells expressing cardiomyocyte marker genes such as myl7. This finding is consistent with previous reports using rtf1 morphants and rtf^1KT64, an ENU-induced point mutation allele (Langenbacher et al., 2011 and Akanuma, 2007). In this revised manuscript, we provide a live image of 2-day-old wild type and rtf1^{LA2679/LA2679} embryos (Fig. 2 Supplement 1). After two days, rtf1 mutant embryos undergo broad cell death. 

(2) Fig. 2, although the in situs are convincing, there is not a quantitative assessment of expression changes for these genes. This could have been done for the bulk or single cell RNA-seq experiments, but was not and these genes weren't not included in the heat maps. A quantitative assessment of these genes would benefit the study. 

The top 40 most significantly diRerentially expressed genes are displayed in the heatmap presented in Fig.5d. The complete diRerential gene expression analysis results for our hand2 FACS-based comparison of rtf1 morphants and controls is presented in Supplementary Data File 1.  In this revised manuscript, we provide a new supplemental figure with violin plots showing the expression levels of genes of interest in our single cell sequencing dataset (Fig.6 Supplement 5).

(3) It doesn't not appear that any statistical tests were used for the comparisons in Fig. 2.

We now provide the statistical data in the legend and Fig.2 b, d, f, h and i.

(4) It's not clear the magnifications and orientations of the embryos in Fig. 3b are the same. 

Embryos shown in Fig.3b are at the same magnification. However, because Rtf1 mutant embryos display severe morphological defects, the orientation of mutant embryos was adjusted to examine the cardiac tissue.

(5) The n's for analysis of MLC2v in WT Rtf1 CKO embryos in Fig. 3b are only 1. At least a few more embryos should be analyzed to confirm that the phenotype is consistent. 

We have revised the figure and present the number of embryos analyzed and statistics in Fig.3c. 

(6) A number of figure panels are referred to out of order in the text. Fig. 4E-G are before Fig. 4C, D, Fig. 7C  before 7B, Fig. 8D-I before 8A ,B. In general, it is easier for the reader if the figures panels are presented in the order they are referred to in the text. 

Revised as suggested.

(7) While additional genes can be included, it is not clear why the same sets of genes are not examined in the bulk or single-cell RNA-seq as with the in situs or expression was analyzed in embryos. I suggest including the genes like nkx2.5, tbx20, myl7, in all the sequencing analysis. 

We used the same set of genes in all analyses when possible. However, the low expression of genes such as nkx2.5 and myl7 in our sc-seq dataset preclude them from the clustering/trajectory analysis. In this revised manuscript, we present violin plots showing their expression in wild type and rtf1 morphants (Fig. 6 Supplement 5).

(8) If a multiomic approach was used, why wasn't its analysis incorporated more into the manuscript? In general, a clearer presentation and deeper analysis of the single cell data would benefit the study. The integration of the RNA and ATAC would benefit the analysis.

As addressed in our response to the reviewer’s public review, both datasets were used in clustering. Examining changes in chromatin accessibility is certainly interesting, but beyond the scope of this study. 

(9) Many of the markers analyzed are not cardiac specific or it is not clear they are expressed in cardiac progenitors at the stage of the analysis. Hand2 has broader expression. Additional confirmation of some of the genes through in situ would help the interpretations. 

Markers used for the in situ hybridization analysis (myl7, mef2ca, nkx2.5, tbx5a, and tbx20) are known for their critical role in heart development. For sc-seq trajectory analyses, most displayed genes (sema3e, bmp6, ttn.2, mef2cb, tnnt2a, ryr2b, and myh7bb) were identified based on their diRerential expression along the LPM-cardiac progenitor pseudotime trajectory. Rather than selecting genes based on their cardiac specificity, our goal was to examine the progressive gene expression changes associated with cardiac progenitor formation and compare gene expression of wild type and rtf1 deficient embryos.

(10) Additional labels of the cell clusters are needed for Supplemental Figs. 2 and 3. 

The cluster IDs were presented on Supplementary Figures 2 and 3. In this revised version, we added predicted cell types to the UMAP (revised Fig.6 Supplement 1) and provided an excel file with this information (revised Supplementary Table 2). 

(11) On lines 101-102, the interpretation from the previous data is that diUerentiation of the LPM requires Rtf1. However, later from the single cell data the interpretation based on the markers is that Rtf1 loss aUects maturation. However, it is not clear this interpretation is correct or what changed from the single cell data. If that were the case, one would expect to see maintenance of more early marks and subsequent loss of maturation markers, which does not appear to the be the case from the presented data.

Our data suggests that cardiac progenitor formation is not accomplished by simultaneously switching on all cardiac marker genes. Our pseudotime trajectory analysis highlights tnnt2a, ryr2b, and myh7bb as genes that increase in expression in a lagged manner compared to mef2cb (Fig. 6). Thus, the abnormal activation of mef2cb without subsequent upregulation of tnnt2a, ryr2b, and myh7bb in rtf1 morphants suggests a requirement for rtf1 in the progressive gene expression changes required for proper cardiac progenitor diRerentiation. Our single cell experiment focuses on the process of cardiac progenitor diRerentiation and does not provide insights into cardiomyocyte maturation. We have edited the text to clarify these interpretations. 

(12) The interpretation that there is not "transfating" is not supported by the shown data. Analysis of markers in other tissues, again with in situ, to show spatially would benefit the study. 

As stated in our response to the reviewer’s public review, we observed a dramatic increase of ALPM cells, but a decrease of ALPM derivatives including the cardiac lineage. We did not observe the expansion of one ALPM-derived subpopulation at the expense of the others. These observations suggest a defect in ALPM diRerentiation and argue against the notion that the region of the ALPM that would normally give rise to cardiac progenitors is instead diRerentiating into another cell type.

(13) The rationale that sequence conservation means a gene is important (lines 137-139) is not really true. There are examples a lot of highly conserved genes whose mutants don't have defects. 

We have revised the text to avoid confusion. 

(14) The data showing that the 8 bp mutations do not aUect the RNA transcript is not shown or at least indicated in Fig. 7. It would seem that this experiment could have been done in the mutant embryos, in which case the experiment would have been semi-blinded as the genotyping would occur after imaging. 

The modified Rtf1 wt RNA (Rtf1 wt* in revised Fig. 7) robustly rescued nkx2.5 expression in rtf1 deficient embryos, demonstrating that the 8 bp modifications do not negatively impact the activity of the injected RNA. As stated previously, morpholino knockdown was used in some experiments because our characterization of rtf1 morphants showed that they faithfully recapitulate the rtf1 mutant phenotype during the timeframe of interest.

(15) Using a technique like PRO-seq at the same stage as the ChIP-seq would complement the ChIP-seq and allow a more detailed analysis of the transcriptional pausing on specific genes observed in WT and mutant embryos. 

As stated in our response to the reviewer’s public review, we appreciate the suggestion but PRO-seq is beyond the scope of this study.

Author response:

The following is the authors’ response to the previous reviews

Public Review:

Reviewer #1 (Public review):

The authors used fluorescence microscopy, image analysis, and mathematical modeling to study the effects of membrane affinity and diffusion rates of MinD monomer and dimer states on MinD gradient formation in B. subtilis. To test these effects, the authors experimentally examined MinD mutants that lock the protein in specific states, including Apo monomer (K16A), ATP-bound monomer (G12V) and ATP-bound dimer (D40A, hydrolysis defective), and compared to wild-type MinD. Overall, the experimental results support the conclusions that reversible membrane binding of MinD is critical for the formation of the MinD gradient, but the binding affinities between monomers and dimers are similar.

The modeling part is a new attempt to use the Monte Carlo method to test the conditions for the formation of the MinD gradient in B. subtilis. The modeling results provide good support for the observations and find that the MinD gradient is sensitive to different diffusion rates between monomers and dimers. This simulation is based on several assumptions and predictions, which raises new questions that need to be addressed experimentally in the future.  

Reviewer #3 (Public review):

This important study by Bohorquez et al examines the determinants necessary for concentrating the spatial modulator of cell division, MinD, at the future site of division and the cell poles. Proper localization of MinD is necessary to bring the division inhibitor, MinC, in proximity to the cell membrane and cell poles

where it prevents aberrant assembly of the division machinery. In contrast to E. coli, in which MinD 50 oscillates from pole-to-pole courtesy of a third protein MinE, how MinD localization is achieved in B. 51 subtilis-which does not encode a MinE analog-has remained largely a mystery. The authors present 52 compelling data indicating that MinD dimerization is dispensable for membrane localization but required 53 for concentration at the cell poles. Dimerization is also important for interactions between MinD and MinC, 54 leading to the formation of large protein complexes. Computational modeling, specifically a Monte Carlo 55 simulation, supports a model in which differences in diffusion rates between MinD monomers and dimers 56 lead to concentration of MinD at cell poles. Once there, interaction with MinC increases the size of the 57 complex, further reinforcing diffusion differences. Notably, interactions with MinJ-which has previously 58 been implicated in MinCD localization, are dispensable for concentrating MinD at cell poles although MinJ may help stabilize the MinCD complex at those locations.

Comments on revisions:  

I believe the authors put respectable effort into revisions and addressing reviewer comments, particularly 64      those that focused on the strengths of the original conclusions. The language in the current version of the manuscript is more precise and the overall product is stronger.  

We are happy to learn that the reviewer considers our manuscript ready for publication.  

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):  

The author has adequately answered the questions that were raised in my previous comments. There are only few minor revisions needed for improvement.  

Line 48−49: 'These proteins ensure that cell division occurs at midcell and not close to nascent division sites or cell poles'  

delete 'nascent division site'  

This has now been corrected as suggested.

Line 64−65: 'MinC inhibits polymerization of FtsZ by direct protein-protein interactions and needs to bind to the Walker A-type ATPase MinD for its recruitment to septa or the polar regions of the cell'

delete 'septa or', because MinD recruits MinC to the cell poles to block polar division, not septal formation.  

This has now been corrected as suggested.

Supplemental information:

Some parameters in Table S1 are missing definitions. If these parameters relate to terms described in the "Methods" section, please add the corresponding parameter symbols after the terms.  

We would like to thank the reviewer for pointing this out. We have improved Table S1 and corrected the related parameters in the Methods section (lines 605-619).

Author response:

Public Reviews:

Reviewer #1 (Public review): 

Summary: 

This manuscript investigates the biological mechanism underlying the assembly and transport of the AcrAB-TolC efflux pump complex. By combining endogenous protein purification with cryo-EM analysis, the authors show that the AcrB trimer adopts three distinct conformations simultaneously and identify a previously uncharacterized lipoprotein, YbjP, as a potential additional component of the complex. The work aims to advance our understanding of the AcrAB-TolC efflux system in near-native conditions and may have broader implications for elucidating its physiological mechanism. 

Strengths: 

Overall, the manuscript is clearly presented, and several of the datasets are of high quality. The use of natively isolated complexes is a major strength, as it minimizes artifacts associated with reconstituted systems and enables the discovery of a novel subunit. The authors also distinguish two major assemblies-the TolC-YbjP sub-complex and the complete pump-which appear to correspond to the closed and open channel states, respectively. The conceptual advance is potentially meaningful, and the findings could be of broad interest to the field. 

Weaknesses: 

(1) As the identification of YbjP is a key contribution of this work, a deeper comparison with functional "anchor" proteins in other efflux pumps is needed. Including an additional supplementary figure illustrating these structural comparisons would be valuable. 

We appreciate this helpful suggestion. We will expand the comparative analysis between YbjP and established anchoring or accessory components in other efflux pumps, and we will add a new supplementary figure illustrating these structural relationships.

(2) The observation of the LTO states in the presence of TolC represents an important extension of previous findings. A more detailed discussion comparing these LTO states to those reported in earlier structural and biochemical studies would improve the clarity and significance of this point. 

We agree. In the revised manuscript we will expand our discussion of the LTO conformations, including a direct comparison with previously reported structural and biochemical observations, to better contextualize the significance of our findings.

Reviewer #2 (Public review): 

Summary: 

This manuscript reports the high-resolution cryo-EM structures of the endogenous TolC-YbjP-AcrABZ complex and a TolC-YbjP subcomplex from E. coli, identifying a novel accessory subunit. This work is an impressive effort that provides valuable structural insights into this native complex. 

Strengths: 

(1) The study successfully determines the structure of the complete, endogenously purified complex, marking a significant achievement. 

(2) The identification of a previously unknown accessory subunit is an important finding. 

(3) The use of cryo-EM to resolve the complex, including potential post-translational modifications such as N-palmitoyl and S-diacylglycerol, is a notable highlight. 

Weaknesses: 

(1) Clarity and Interpretation: Several points need clarification. Additionally, the description of the sample preparation method, which is a key strength, is currently misplaced and should be introduced earlier. 

Thank you for pointing this out. We will reorganize the text to introduce the sample preparation strategy earlier and clarify the points that may cause ambiguity.

(2) Data Presentation: The manuscript would benefit significantly from improved figures. 

We agree and will revise the figures to improve clarity, consistency, and readability. Additional schematic illustrations will also be included where appropriate.

(3) Supporting Evidence: The inclusion of the protein purification profile as a supplementary figure is essential. Furthermore, a discussion comparing the endogenous AcrB structure to those obtained in other systems (e.g., liposomes) and commenting on observed lipid densities would strengthen the overall analysis. 

We appreciate these suggestions. We will add the purification profile and expand the comparison between our endogenous AcrB structure and previously reported structures from reconstituted systems, including a more detailed discussion of lipid densities.

Reviewer #3 (Public review): 

Summary: 

The manuscript "Structural mechanisms of pump assembly and drug transport in the AcrAB-TolC efflux system" by Ge et al. describes the identification of a previously uncharacterized lipoprotein, YbjP, as a novel partner of the well-studied Enterobacterial tripartite efflux pump AcrAB-TolC. The authors present cryo-electron microscopy structures of the TolC-YbjP subcomplex and the complete AcrABZ-TolC-YbjP assembly. While the identification and structural characterization of YbjP are potentially novel, the stated focus of the manuscript-mechanisms of pump assembly and drug transport - is not sufficiently addressed. The manuscript requires reframing to emphasize the principal novelty associated with YbjP and significant development of the other aspects, especially the claimed novelty of the AcrB drug-efflux cycle. 

Strengths: 

The reported association of YbjP with AcrAB-TolC is novel; however, a recent deposition of a preceding and much more detailed manuscript to the BioRxiv server (Horne et al., https://doi.org/10.1101/2025.03.19.644130) removes much of the immediate novelty. 

Weaknesses: 

While the identification of YbjP is novel, the authors do not appear to acknowledge the precedence of another work (Horne et al., 2025), and it is not cited within the correct context in the manuscript. 

We thank the reviewer for rasising this important point regarding the independent nature of our work.

Our study indeed progressed independently. The process began with our purification of an endogenous protein sample containing the AcrAB-TolC efflux pump. During our cryo-EM analysis, we observed an unassigned density in the map, for which we built a preliminary main-chain model. A subsequent search of structural databases, including AlphaFold predictions, allowed us to identify this density as the protein YbjP. It was only after this identification that we became aware of the related preprint by Horne et al. on BioRxvi (Posted March 19, 2025).

Therefore, our structural determination of YbjP was conducted entirely independently. We fully acknowledge and respect the work by Horne et al. and have already cited their reprint in our manuscript. While their detailed structural data, maps, and coordinates are not yet publicly available, we have described their findings appropriately. We agree that our manuscript can better reflect this context and will carefully check for any missing citations to ensure that their contribution is properly and clearly acknowledged.

We also believe that the two studies are mutually complementary and collectively reinforce the emerging understanding of YbjP.

Several results presented in the TolC-YbjP section do not represent new findings regarding TolC structure itself.

We agree that the TolC features we describe are consistent with previously reported structural characteristics. However, these observations could only be confirmed in the context of the newly determined TolC–YbjP subcomplex, which was not available prior to this study. We will clarify this point in the revision to avoid overstating novelty.

The structure and gating behaviour of TolC should be more thoroughly introduced in the Introduction, including prior work describing channel opening and conformational transitions.

We appreciate this suggestion and agree that a more comprehensive overview of TolC gating and conformational transitions will strengthen the Introduction. We will revise the text to incorporate relevant prior structural and functional studies.

The current manuscript does not discuss the mechanistic role of helices H3/H4 and H7/H8 in channel dilation, despite implying that YbjP binding may influence these features.

Thank you for this comment. The primary novel contributions of this manuscript are the identification of YbjP and the structural characterization of AcrB in three distinct states. The discussion of the dilation mechanism, while included because we observed the closed TolC-YbjP state, is a secondary point. In the revised manuscript, we will expand this discussion as suggested.

Only the original closed TolC structure is cited, and the manuscript does not address prior mutational studies involving the D396 region, though this residue is specifically highlighted in the presented structures. 

We appreciate the reviewer drawing attention to this oversight. We will add citations to the relevant mutational and mechanistic studies, including those involving the D396 region, and more clearly discuss these findings in relation to our structural observations.

The manuscript provides only a general structural alignment between the closed TolC-YbjP subcomplex and the open TolC observed in the full pump assembly. However, multiple open, closed, and intermediate conformations of AcrAB-TolC have already been reported. Thus, YbjP alone cannot be assumed to account for TolC channel gating. A systematic comparison with existing structures is necessary to determine whether YbjP contributes any distinct allosteric modulation. 

We agree with the reviewer’s assessment and appreciate the constructive suggestion. In our revised manuscript, we will expand the structural comparison to include previously reported open, closed, and intermediate AcrAB–TolC conformations. This expanded analysis will more clearly position our findings within the existing structural framework.

The analysis of AcrB peristaltic action is superficial, poorly substantiated and importantly, not novel. Several references to the ATP-synthase cycle have been provided, but this has been widely established already some 20 years ago - e.g. https://www.science.org/doi/10.1126/science.1131542. 

We thank the reviewer for this comment. We fully acknowledge the foundational studies that established the AcrB functional cycle and its analogy to the ATP-synthase mechanism. While previous work indeed defined the LTO (Loose, Tight, Open) cycle of AcrB, those structures were obtained using AcrB in isolation. In contrast, our endogenous sample, which includes the native constraints of AcrA from above and the presence of AcrZ, reveals conformational changes in the transmembrane and porter domains that differ from those previously reported. We interpret these differences as reflecting a more physiologically relevant mechanism. In our revision, we will provide a detailed discussion to contextualize these distinctions within the existing literature.

The most significant limitation of the study is the absence of functional characterization of YbjP in vivo or in vitro. While the structural association between YbjP and TolC is interesting, the biological role of YbjP remains unclear.

We agree that the lack of functional characterization is a limitation of the present work. Our study focuses on structural elucidation and structural analysis. Although the recent preprint you mentioned suggests that YbjP deletion may not produce a strong phenotype, we are still interested in conducting additional experiments to explore its potential roles in future work. We will revise the text to clearly acknowledge this limitation.

Moreover, the manuscript does not examine structural differences between the presented complex and previously solved AcrAB-TolC or MexAB-OprM assemblies that might support a mechanistic model.

We thank the reviewer for this suggestion. We will incorporate a more detailed comparative analysis with existing AcrAB–TolC and MexAB–OprM structures and highlight similarities and differences that may inform mechanistic interpretation.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript by Lu and colleagues demonstrates convincingly that PRRT2 interacts with brain voltage-gated sodium channels to enhance slow inactivation in vitro and in vivo. The work is interesting and rigorously conducted. The relevance to normal physiology and disease pathophysiology (e.g., PRRT2-related genetic neurodevelopmental disorders) seems high. Some simple additional experiments could elevate the impact and make the study more complete.

Strengths:

Experiments are conducted rigorously, including experimenter blinding and appropriate controls. Data presentation is excellent and logical. The paper is well written for a general scientific audience.

Weaknesses:

There are a few missing experiments and one place where data are over-interpreted.

(1) An in vitro study of Nav1.6 is conspicuously absent. In addition to being a major brain Na channel, Nav1.6 is predominant in cerebellar Purkinje neurons, which the authors note lack PRRT2 expression. They speculate that the absence of PRRT2 in these neurons facilitates the high firing rate. This hypothesis would be strengthened if PRRT2 also enhanced slow inactivation of Nav1.6. If a stable Nav1.6 cell were not available, then simple transient co-transfection experiments would suffice.

We thank the reviewer for this suggestion. In the revised manuscript, we will examine whether PRRT2 modulates slow inactivation of Nav1.6 channels using heterologous co-expression experiments.

(2) To further demonstrate the physiological impact of enhanced slow inactivation, the authors should consider a simple experiment in the stable cell line experiments (Figure 1) to test pulse frequency dependence of peak Na current. One would predict that PRRT2 expression will potentiate 'run down' of the channels, and this finding would be complementary to the biophysical data.

We agree that examining pulse frequency-dependent changes in peak sodium current would provide a functional readout linking PRRT2-mediated enhancement of slow inactivation to use-dependent channel availability. In the revision, we will include a pulse-train protocol to quantify use-dependent attenuation (“run-down”) of peak sodium current across stimulation trains and will compare this adaptation between control and PRRT2-expressing conditions.

(3) The study of one K channel is limited, and the conclusion from these experiments represents an over-interpretation. I suggest removing these data unless many more K channels (ideally with measurable proxies for slow inactivation) were tested. These data do not contribute much to the story.

We agree with the reviewer’s assessment. To avoid over-interpretation and to maintain focus on PRRT2-dependent regulation of Nav channel slow inactivation, we will remove potassium channel dataset and the associated conclusions from the revised manuscript.

(4) In Figure 2, the authors should confirm that protein is indeed expressed in cells expressing each truncated PRRT2 construct. Absent expression should be ruled out as an explanation for the enhancement of slow inactivation.

We appreciate the reviewer’s concern regarding expression of the truncated PRRT2 constructs in the Nav1.2 stable cell line, particularly PRRT2(1-266), which shows little effect on slow inactivation of Nav1.2 channels. In the revision, we will include expression controls for each truncation construct in the Nav1.2-expressing cells to rule out lack of expression as an explanation for the observed functional differences.

Reviewer #2 (Public review):

Summary:

As a member of DspB subfamily, PRRT2 is primarily expressed in the nervous system and has been associated with various paroxysmal neurological disorders. Previous studies have shown that PRRT2 directly interacts with Nav1.2 and Nav1.6, modulating channel properties and neuronal excitability.

In this study, Lu et al. reported that PRRT2 is a physiological regulator of Nav channel slow inactivation, promoting the development of Nav slow inactivation and impeding the recovery from slow inactivation. This effect can be replicated by the C-terminal region (256-346) of PRRT2, and is highly conserved across species from zebrafish, mouse, to human PRRT2. TRARG1 and TMEM233, the other two DspB family members, showed similar effects on Nav1.2 slow inactivation. Co-IP data confirms the interaction between Nav channels and PRRT2. Prrt2-mutant mice, which lack PRRT2 expression, require lower stimulation thresholds for evoking after-discharges when compared to WT mice.

Strengths:

(1) This study is well designed, and data support the conclusion that PRRT2 is a potent regulator of slow inactivation of Nav channels.

(2) This study reveals similar effects on Nav1.2 slow inactivation by PRRT2, TMEM233, and TRARG1, indicating a common regulation of Nav channels by DspB family members (Supplemental Figure 2). A recent study has shown that TMEM233 is essential for ExTxA (a plant toxin)-mediated inhibition on fast inactivation of Nav channels; and PRRT2 and TRARG1 could replicate this effect (Jami S, et al. Nat Commun 2023). It is possible that all three DspB members regulate Nav channel properties through the same mechanism, and exploring molecules that target PRRT2/TRARG1/TMEM233 might be a novel strategy for developing new treatments of DspB-related neurological diseases.

Weaknesses:

(1) Previously, the authors have reported that PRRT2 reduces Nav1.2 current density and alters biophysical properties of both Nav1.2 and Nav1.6 channels, including enhanced steady-state inactivation, slower recovery, and stronger use-dependent inhibition (Lu B, et al. Cell Rep 2021, Fig 3 & S5). All those changes are expected to alter neuronal excitability and should be discussed.

We agree that PRRT2 has been reported to exert multiple effects on Nav channels which are all expected to influence neuronal excitability (Fruscione et al., 2018; Lu et al., 2021; Valente et al., 2023). In the revised manuscript, we will expand the Discussion to integrate these prior findings and to clarify how these PRRT2-dependent changes may interact with (and potentially converge on) modulation of slow inactivation to shape neuronal excitability.

(2) In this study, the fast inactivation kinetics was examined by a single stimulus at 0 mV, which may not be sufficient for the conclusion. Inactivation kinetics at more voltage potentials should be added.

We thank the reviewer for this suggestion. In the revision, we will extend our analysis of Nav1.2 fast-inactivation kinetics across a range of test potentials (e.g., -20, -10, 0, +10 and +20 mV) in the presence and absence of PRRT2.

(3) It is a little surprising that there is no difference in Nav1.2 current density in axon-blebs between WT and Prrt2-mutant mice (Figure 7B). PRRT2 significantly shifts steady-state slow inactivation curve to hyperpolarizing direction, at -70 mV, nearly 70% of Nav1.2 channels are inactivated by slow inactivation in cells expressing PRRT2 when compared to less than 10% in cells expressing GFP (Figure supplement 1B); with a holding potential of -70 mV, I would expect that most of Nav channels are inactivated in axon-blebs from WT mice but not in axon-blebs from Prrt2-mutant mice, and therefore sodium current density should be different in Figure 7B, which was not. Any explanation?

We appreciate the reviewer for raising this point. In our axonal bleb recordings, although the holding potential was -70 mV, sodium current density was measured after a hyperpolarizing pre-pulse (-110 mV) to relieve inactivation immediately prior to the test depolarization (as described in the Methods). Thus, the current density measurement in Figure 7B reflects the maximal available current following this recovery step, rather than the steady-state availability at -70 mV. In the revision, we will state this explicitly in the Results and/or figure legend to avoid confusion.

(4) Besides Nav channels, PRRT2 has been shown to act on Cav2.1 channels as well as molecules involved in neurotransmitter release, which may also contribute to abnormal neuronal activity in Prrt2-mutant mice. These should be mentioned when discussing PRRT2's role in neuronal resilience.

We agree with the reviewer. In the revised manuscript, we will broaden the Discussion to acknowledge PRRT2 functions beyond Nav channels, including reported roles in Cav2.1 regulation and neurotransmitter release. We will frame the in vivo phenotypes in Prrt2-mutant mice as likely arising from convergent mechanisms—altered intrinsic excitability together with changes in synaptic transmission.

Reviewer #3 (Public review):

This paper reveals that the neuronal protein PRRT2, previously known for its association with paroxysmal dyskinesia and infantile seizures, modulates the slow inactivation of voltage-gated sodium ion (Nav) channels, a gating process that limits excitability during prolonged activity. Using electrophysiology, molecular biology, and mouse models, the authors show that PRRT2 accelerates entry of Nav channels into the slow-inactivated state and slows their recovery, effectively dampening excessive excitability. The effect seems evolutionarily conserved, requires the C-terminal region of PRRT2, and is recapitulated in cortical neurons, where PRRT2 deficiency leads to hyper-responsiveness and reduced cortical resilience in vivo. These findings extend the functional repertoire of PRRT2, identifying it as a physiological brake on neuronal excitability. The work provides a mechanistic link between PRRT2 mutations and episodic neurological phenotypes.

Comments:

(1) The precise structural interface and the molecular basis of gating modulation remain inferred rather than demonstrated.

We thank the reviewer for this comment. In the revision, we will make it explicit that our structural modeling are based on prediction rather than evidential. We will also expand the Limitations section to highlight that direct structural and biochemical mapping of the PRRT2-Nav interface (e.g., through targeted mutagenesis, crosslinking, and/or structural determination) will be required to define the binding interface and establish the molecular basis of gating modulation.

(2) The in vivo phenotype reflects a complex circuit outcome and does not isolate slow-inactivation defects per se.

We agree with the reviewer. In the revision, we will refine the Discussion to avoid over-attributing the in vivo phenotype to slow-inactivation defects alone and to explicitly state that impaired slow inactivation in Prrt2-mutant mice represents one plausible contributing mechanism to reduced cortical resilience, alongside other PRRT2-dependent process.

(3) Expression of PRRT2 in muscle or heart is low, so the cross-isoform claims are likely of limited physiological significance.

We thank the review for your comment about physiological relevance. In the revised manuscript, we will clarify that our Nav isoform panel was designed to assess mechanistic generality at the channel level rather than to imply broad in vivo relevance across tissues. We will also expand the Discussion to emphasize that any therapeutic strategy involving PRRT2 delivery should consider its consistent effect on slow inactivation across multiple Nav isoforms.

(4) The mechanistic separation between the trafficking effect of PRRT2 and its gating effects is not clearly resolved.

We appreciate the reviewer for raising this important point. In the revision, we will expand the Discussion to clarify why we interpret the effect of PRRT2 on slow inactivation as a gating modulation rather than a secondary consequence of altered channel abundance or localization. First, our slow inactivation measurements are expressed as the fraction of available channels after depolarization conditioning relative to baseline availability within the same cell (post-/pre-conditioning), which minimizes confounding by differences in initial surface expression. Second, the slow inactivation of Nav channel occurs on a rapid, activity-dependent timescale (seconds), whereas remarkable changes in trafficking and surface abundance generally develop over longer intervals (minutes to hours).

(5) Additional studies with Nav1.6 should be carried out.

We thank the reviewer’s suggestion. We will include Nav1.6 slow inactivation experiments in the revised manuscript.

Author response:

eLife Assessment

This important study fills a major geographic and temporal gap in understanding Paleocene mammal evolution in Asia and proposes an intriguing "brawn before bite" hypothesis grounded in diverse analytical approaches. However, the findings are incomplete because limitations in sampling design - such as the use of worn or damaged teeth, the pooling of different tooth positions, and the lack of independence among teeth from the same individuals - introduce uncertainties that weaken support for the reported disparity patterns. The taxonomic focus on predominantly herbivorous clades also narrows the ecological scope of the results. Clarifying methodological choices, expanding the ecological context, and tempering evolutionary interpretations would substantially strengthen the study.

We thank Dr. Rasmann for the constructive evaluation of our manuscript. Considering the reviewers’ comments, we plan to implement revisions to our study focusing on (1) expansion of the fossil sample description, including a detailed account of the process of excluding extremely worn or damaged teeth from all analyses, (2) expanded reporting of the analyses done on individual tooth positions, and tempering the interpretation of the pooled samples in light of the issues raised by reviewers, (3) providing a more comprehensive introduction that includes an overview of the Paleocene mammal faunas in south China, which unevenly samples certain clades whereas others are extremely rare, and why the current available fossil samples would not permit a whole-fauna analysis to be adequately conducted across the three land mammal age time bins of the Paleocene in China. We believe these revisions would substantially strengthen the study’s robustness and impact for understanding the ecomorphological evolution of the earliest abundant placental mammals during the Paleocene in Asia.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work provides valuable new insights into the Paleocene Asian mammal recovery and diversification dynamics during the first ten million years post-dinosaur extinction. Studies that have examined the mammalian recovery and diversification post-dinosaur extinction have primarily focused on the North American mammal fossil record, and it's unclear if patterns documented in North America are characteristic of global patterns. This study examines dietary metrics of Paleocene Asian mammals and found that there is a body size disparity increase before dietary niche expansion and that dietary metrics track climatic and paleobotanical trends of Asia during the first 10 million years after the dinosaur extinction.

Strengths:

The Asian Paleocene mammal fossil record is greatly understudied, and this work begins to fill important gaps. In particular, the use of interdisciplinary data (i.e., climatic and paleobotanical) is really interesting in conjunction with observed dietary metric trends.

Weaknesses:

While this work has the potential to be exciting and contribute greatly to our understanding of mammalian evolution during the first 10 million years post-dinosaur extinction, the major weakness is in the dental topographic analysis (DTA) dataset.

There are several specimens in Figure 1 that have broken cusps, deep wear facets, and general abrasion. Thus, any values generated from DTA are not accurate and cannot be used to support their claims. Furthermore, the authors analyze all tooth positions at once, which makes this study seem comprehensive (200 individual teeth), but it's unclear what sort of noise this introduces to the study. Typically, DTA studies will analyze a singular tooth position (e.g., Pampush et al. 2018 Biol. J. Linn. Soc.), allowing for more meaningful comparisons and an understanding of what value differences mean. Even so, the dataset consists of only 48 specimens. This means that even if all the specimens were pristinely preserved and generated DTA values could be trusted, it's still only 48 specimens (representing 4 different clades) to capture patterns across 10 million years. For example, the authors note that their results show an increase in OPCR and DNE values from the middle to the late Paleocene in pantodonts. However, if a singular tooth position is analyzed, such as the lower second molar, the middle and late Paleocene partitions are only represented by a singular specimen each. With a sample size this small, it's unlikely that the authors are capturing real trends, which makes the claims of this study highly questionable.

We thank Reviewer 1 for their careful review of our manuscript. A major external limitation of the application of DTA to fossil samples is the availability of specimens. Whereas a typical study design using extant or geologically younger/more abundant fossil species would preferably sample much larger quantities of teeth from each treatment group (time bins, in our case), the rarity of well-preserved Paleocene mammalian dentitions in Asia necessitates the analysis of small samples in order to make observations regarding major trends in a region and time period otherwise impossible to study (see Chow et al. 1977). That said, we plan to clarify methodological details in response to the reviewer’s comments, including a more comprehensive explanation of our criteria for exclusion of broken tooth crowns from the analyses. We also plan to expand our results reporting on individual tooth position analysis, potentially including resampling and/or simulation analyses to assess the effect of small and uneven samples on our interpretation of results. Lastly, we plan to revise the discussion and conclusion accordingly, including more explicit distinction between well-supported findings that emerge from various planned sensitivity analyses, versus those that are more speculative and tentative in nature.

Chow, M., Zhang, Y., Wang, B., and Ding, S. (1977). Paleocene mammalian fauna from the Nanxiong Basin, Guangdong Province. Paleontol. Sin. New Ser. C 20, 1–100.

Reviewer #2 (Public review):

Summary:

This study uses dental traits of a large sample of Chinese mammals to track evolutionary patterns through the Paleocene. It presents and argues for a 'brawn before bite' hypothesis - mammals increased in body size disparity before evolving more specialized or adapted dentitions. The study makes use of an impressive array of analyses, including dental topographic, finite element, and integration analyses, which help to provide a unique insight into mammalian evolutionary patterns.

Strengths:

This paper helps to fill in a major gap in our knowledge of Paleocene mammal patterns in Asia, which is especially important because of the diversification of placentals at that time. The total sample of teeth is impressive and required considerable effort for scanning and analyzing. And there is a wealth of results for DTA, FEA, and integration analyses. Further, some of the results are especially interesting, such as the novel 'brawn before bite' hypothesis and the possible link between shifts in dental traits and arid environments in the Late Paleocene. Overall, I enjoyed reading the paper, and I think the results will be of interest to a broad audience.

Weaknesses:

I have four major concerns with the study, especially related to the sampling of teeth and taxa, that I discuss in more detail below. Due to these issues, I believe that the study is incomplete in its support of the 'brawn before bite' hypothesis. Although my concerns are significant, many of them can be addressed with some simple updates/revisions to analyses or text, and I try to provide constructive advice throughout my review.

(1) If I understand correctly, teeth of different tooth positions (e.g., premolars and molars), and those from the same specimen, are lumped into the same analyses. And unless I missed it, no justification is given for these methodological choices (besides testing for differences in proportions of tooth positions per time bin; L902). I think this creates some major statistical concerns. For example, DTA values for premolars and molars aren't directly comparable (I don't think?) because they have different functions (e.g., greater grinding function for molars). My recommendation is to perform different disparity-through-time analyses for each tooth position, assuming the sample sizes are big enough per time bin. Or, if the authors maintain their current methods/results, they should provide justification in the main text for that choice.

We thank Reviewer 2 for raising several issues worthy of clarification. Separate analyses for individual tooth positions were performed but not emphasized in the first version of the study. In our revised version we plan to highlight the nuances of the results from premolar versus molar partition analyses.

Also, I think lumping teeth from the same specimen into your analyses creates a major statistical concern because the observations aren't independent. In other words, the teeth of the same individual should have relatively similar DTA values, which can greatly bias your results. This is essentially the same issue as phylogenetic non-independence, but taken to a much greater extreme.

It seems like it'd be much more appropriate to perform specimen-level analyses (e.g., Wilson 2013) or species-level analyses (e.g., Grossnickle & Newham 2016) and report those results in the main text. If the authors believe that their methods are justified, then they should explain this in the text.

We plan to emphasize individual tooth position analyses in our revisions, and provide a stronger justification for our current treatment of multiple teeth from the same individual specimens as independent samples. We recognize the statistical nonindependence raised by Reviewer 2, but we would point out that from an ecomorphological perspective, it is unclear to us that the heterodont dentition of these early Cenozoic placental mammals should represent a single ecological signal (and thus warrant using only a single tooth position as representative of an individual’s DTA values). We plan to closely examine the nature of nonindependence in the DTA data within individuals, to assess a balanced approach to maximize information content from the relatively small and rare fossil samples used, while minimizing signal nonindependence across the dentition.

(2) Maybe I misunderstood, but it sounds like the sampling is almost exclusively clades that are primarily herbivorous/omnivorous (Pantodonta, Arctostylopida, Anagalida, and maybe Tillodonta), which means that the full ecomorphological diversity of the time bins is not being sampled (e.g., insectivores aren't fully sampled). Similarly, the authors say that they "focused sampling" on those major clades and "Additional data were collected on other clades ... opportunistically" (L628). If they favored sampling of specific clades, then doesn't that also bias their results?

If the study is primarily focused on a few herbivorous clades, then the Introduction should be reframed to reflect this. You could explain that you're specifically tracking herbivore patterns after the K-Pg.

We plan to revise the introduction section to more accurately reflect the emphasis on those clades. However, we would note that conventional dietary ecomorphology categories used to characterize later branching placental mammals are likely to be less informative when applied to their Paleocene counterparts. Although there are dental morphological traits that began to characterize major placental clades during the Paleocene, distinctive dietary ecologies have not been demonstrated for most of the clade representatives studied. Thus, insectivory was probably not restricted to “Insectivora”, nor carnivory to early Carnivmorpha or “Creodonta”, each of which represented less than 5% of the taxonomic richness during the Paleocene in China (Wang et al. 2007).

Wang, Y., Meng, J., Ni, X., and Li, C. (2007). Major events of Paleogene mammal radiation in China. Geol. J. 42, 415–430.

(3) There are a lot of topics lacking background information, which makes the paper challenging to read for non-experts. Maybe the authors are hindered by a short word limit. But if they can expand their main text, then I strongly recommend the following:

(a) The authors should discuss diets. Much of the data are diet correlates (DTA values), but diets are almost never mentioned, except in the Methods. For example, the authors say: "An overall shift towards increased dental topographic trait magnitudes ..." (L137). Does that mean there was a shift toward increased herbivory? If so, why not mention the dietary shift? And if most of the sampled taxa are herbivores (see above comment), then shouldn't herbivory be a focal point of the paper?

We plan to revise the text to make clearer connections between DTA and dietary inferences, and at the same time advise caution in making one-to-one linkages between them. Broadly speaking, dental indices such as DTA are phenotypic traits, and as in other phenotypic traits, the strength of structure-function relationships needs to be explicitly established before dietary ecological inferences can be confidently made. There is, to date, no consistent connection between dental topology and tooth use proxies and biomechanical traits in extant non-herbivorous species (e.g., DeSantis et al. 2017, Tseng and DeSantis 2024), and in our analyses, FEA and DTA generally did not show strong correlations to each other. Thus, we plan to continue to exercise care in interpreting DTA data as dietary data.

DeSantis LRG, Tseng ZJ, Liu J, Hurst A, Schubert BW, Jiangzuo Q. Assessing niche conservatism using a multiproxy approach: dietary ecology of extinct and extant spotted hyenas. Paleobiology. 2017;43(2):286-303. doi:10.1017/pab.2016.45

Tseng ZJ, DeSantis LR. Relationship between tooth macrowear and jaw morphofunctional traits in representative hypercarnivores. PeerJ. 2024 Nov 11;12:e18435.

(b) The authors should expand on "we used dentitions as ecological indicators" (L75). For non-experts, how/why are dentitions linked to ecology? And, again, why not mention diet? A strong link between tooth shape and diet is a critical assumption here (and one I'm sure that all mammalogists agree with), but the authors don't provide justification (at least in the Introduction) for that assumption. Many relevant papers cited later in the Methods could be cited in the Introduction (e.g., Evans et al. 2007).

Thank you for this suggestion. We plan to expand the introduction section to better contextualize the methodological basis for the work presented.

(c) Include a better introduction of the sample, such as explicitly stating that your sample only includes placentals (assuming that's the case) and is focused on three major clades. Are non-placentals like multituberculates or stem placentals/eutherians found at Chinese Paleocene fossil localities and not sampled in the study, or are they absent in the sampled area?

We thank Reviewer 2 for raising this important point worthy of clarification. Multituberculates are completely absent from the first two land mammal ages in the Paleocene of Asia, and non-placentals are rare in general (Wang et al. 2007). We plan to provide more context for the taxonomic sampling choices made in the study.

Wang, Y., Meng, J., Ni, X., and Li, C. (2007). Major events of Paleogene mammal radiation in China. Geol. J. 42, 415–430.

(d) The way in which "integration" is being used should be defined. That is a loaded term which has been defined in different ways. I also recommend providing more explanation on the integration analyses and what the results mean.

If the authors don't have space to expand the main text, then they should at least expand on the topics in the supplement, with appropriate citations to the supplement in the main text.

We plan to clarify our usage of “integration” to enable readers to accurately interpret what we mean by it.

(4) Finally, I'm not convinced that the results fully support the 'brawn before bite' hypothesis. I like the hypothesis. However, the 'brawn before ...' part of the hypothesis assumes that body size disparity (L63) increased first, and I don't think that pattern is ever shown. First, body size disparity is never reported or plotted (at least that I could find) - the authors just show the violin plots of the body sizes (Figures 1B, S6A). Second, the authors don't show evidence of an actual increase in body size disparity. Instead, they seem to assume that there was a rapid diversification in the earliest Paleocene, and thus the early Paleocene bin has already "reached maximum saturation" (L148). But what if the body size disparity in the latest Cretaceous was the same as that in the Paleocene? (Although that's unlikely, note that papers like Clauset & Redner 2009 and Grossnickle & Newham 2016 found evidence of greater body size disparity in the latest Cretaceous than is commonly recognized.) Similarly, what if body size disparity increased rapidly in the Eocene? Wouldn't that suggest a 'BITE before brawn' hypothesis? So, without showing when an increase in body size diversity occurred, I don't think that the authors can make a strong argument for 'brawn before [insert any trait]".

Although it's probably well beyond the scope of the study to add Cretaceous or Eocene data, the authors could at least review literature on body size patterns during those times to provide greater evidence for an earliest Paleocene increase in size disparity.

We plan to provide a broader discussion and any supporting evidence from the Cretaceous and Eocene to either make a stronger case for “brawn before bite”, or to refine what we mean by brawn/size/size disparity.

Author response:

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

eLife Assessment

This Review Article explores the intricate relationship between humans and Mycobacterium tuberculosis (Mtb), providing an additional perspective on TB disease. Specifically, this review focuses on the utilization of systems-level approaches to study TB, while highlighting challenges in the frameworks used to identify the relevant immunologic signals that may explain the clinical spectrum of disease. The work could be further enhanced by better defining key terms that anchor the review, such as "unified mechanism" and "immunological route." This review will be of interest to immunologists as well as those interested in evolution and host-pathogen interactions.

We thank the editors for reviewing our article and for the primarily positive comments. We accept that better definition and terminology will improve the clarity of the message, and so have changed the wording as suggested above in the revised manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This is an interesting and useful review highlighting the complex pathways through which pulmonary colonisation or infection with Mycobacterium tuberculosis (Mtb) may progress to develop symptomatic disease and transmit the pathogen. I found the section on immune correlates associated with individuals who have clearly been exposed to and reacted to Mtb but did not develop latent infections particularly valuable. However, several aspects would benefit from clarification.

Strengths:

The main strengths lie in the arguments presented for a multiplicity of immune pathways to TB disease.

Weaknesses:

The main weaknesses lie in clarity, particularly in the precise meanings of the three figures.

We accept this point, and have completely changed figure 2, and have expanded the legends for figure 1 and 3 to maximise clarity.

I accept that there is a 'goldilocks zone' that underpins the majority of TB cases we see and predominantly reflects different patterns of immune response, but the analogies used need to be more clearly thought through.

We are glad the reviewer agrees with the fundamental argument of different patterns of immunity, and have revised the manuscript throughout where we feel the analogies could be clarified.

Reviewer #2 (Public review):

Summary:

This is a thought-provoking perspective by Reichmann et al, outlining supportive evidence that Mycobacterium tuberculosis co-evolved with its host Homo Sapiens to both increase susceptibility to infection and reduce rates of fatal disease through decreased virulence. TB is an ancient disease where two modes of virulence are likely to have evolved through different stages of human evolution: one before the Neolithic Demographic Transition, where humans lived in sparse hunter-gatherer communities, which likely selected for prolonged Mtb infection with reduced virulence to allow for transmission across sparse populations. Conversely, following the agricultural and industrial revolutions, Mtb virulence is likely to have evolved to attack a higher number of susceptible individuals. These different disease modalities highlight the central idea that there are different immunological routes to TB disease, which converge on a disease phenotype characterized by high bacterial load and destruction of the extracellular matrix. The writing is very clear and provides a lot of supportive evidence from population studies and the recent clinical trials of novel TB vaccines, like M72 and H56. However, there are areas to support the thesis that have been described only in broad strokes, including the impact of host and Mtb genetic heterogeneity on this selection, and the alternative model that there are likely different TB diseases (as opposed to different routes to the same disease), as described by several groups advancing the concept of heterogeneous TB endotypes. I expand on specific points below.

Strengths:

The idea that Mtb evolved to both increase transmission (and possible commensalism with humans) with low rates of reactivation is intriguing. The heterogeneous TB phenotypes in the collaborative cross model (PMID: 35112666) support this idea, where some genetic backgrounds can tolerate a high bacterial load with minimal pathology, while others show signs of pathogenesis with low bacterial loads. This supports the idea that the underlying host state, driven by a number of factors like genetics and nutrition, is likely to explain whether someone will co-exist with Mtb without pathology, or progress to disease. I particularly enjoyed the discussion of the protective advantages provided by Mtb infection, which may have rewired the human immune system to provide protection against heterologous pathogens- this is supported by recent studies showing that Mtb infection provides moderate protection against SARS-CoV-2 (PMID: 35325013, and 37720210), and may have applied to other viruses that are likely to have played a more significant role in the past in the natural selection of Homo Sapiens.

We thank the reviewer for their positive comments, and also for pointing out work that we have overlooked citing previously. We now discuss and cite the work above as suggested

Modeling from Marcel Behr and colleagues (PMID: 31649096) indeed suggests that there are at least TB clinical phenotypes that likely mirror the two distinct phases of Mtb co-evolution with humans. Most of the TB disease progression occurs rapidly (within 1-2 years of exposure), and the rest are slow cases of reactivation over time. I enjoyed the discussion of the difference between the types of immune hits needed to progress to disease in the two scenarios, where you may need severe immune hits for rapid progression, a phenotype that likely evolved after the Neolithic transition to larger human populations. On the other hand, a series of milder immune events leading to reactivation after a long period of asymptomatic infection likely mirrors slow progression in the hunter-gatherer communities, to allow for prolonged transmission in scarce populations. Perhaps a clearer analysis of these models would be helpful for the reader.

We agree that we did not present these concepts in as much detail as we should, and so we now discuss this more on lines 81 – 83 and 184 - 187)

Weaknesses:

The discussion of genetic heterogeneity is limited and only discusses evidence from MSMD studies. Genetics is an important angle to consider in the co-evolution of Mtb and humans. There is a large body of literature on both host and Mtb genetic associations with TB disease. The very fact that host variants in one population do not necessarily cross-validate across populations is evidence in support of population-specific adaptations. Specific Mtb lineages are likely to have co-evolved with distinct human populations. A key reference is missing (PMID: 23995134), which shows that different lineages co-evolved with human migrations. Also, meta-analyses of human GWAS studies to define variants associated with TB are very relevant to the topic of co-evolution (e.g., PMID: 38224499). eQTL studies can also highlight genetic variants associated with regulating key immune genes involved in the response to TB. The authors do mention that Mtb itself is relatively clonal with ~2K SNPs marking Mtb variation, much of which has likely evolved under the selection pressure of modern antibiotics. However, some of this limited universe of variants can still explain co-adaptations between distinct Mtb lineages and different human populations, as shown recently in the co-evolution of lineage 2 with a variant common in Peruvians (PMID: 39613754).

We thank the reviewer for these comments and agree we failed to cite and discuss the work from Sebastian Gagneux’s group on co-migration, which we now discuss. We include a new paragraph discussing co-evolution as suggested on lines 145 – 155 and 218 -220 , citing the work proposed, which we agree enhances the arguments about co-evolution.

Although the examples of anti-TNF and anti-PD1 treatments are relevant as drivers of TB in limited clinical contexts, the bigger picture is that they highlight major distinct disease endotypes. These restricted examples show that TB can be driven by immune deficiency (as in the case of anti-TNF, HIV, and malnutrition) or hyperactivation (as in the case of anti-PD1 treatment), but there are still certainly many other routes leading to immune suppression or hyperactivation. Considering the idea of hyper-activation as a TB driver, the apparent higher rate of recurrence in the H56 trial referenced in the review is likely due to immune hyperactivation, especially in the context of residual bacteria in the lung. These different TB manifestations (immune suppression vs immune hyperactivation) mirror TB endotypes described by DiNardo et al (PMID: 35169026) from analysis of extensive transcriptomic data, which indicate that it's not merely different routes leading to the same final endpoint of clinical disease, but rather multiple different disease endpoints. A similar scenario is shown in the transcriptomic signatures underlying disease progression in BCG-vaccinated infants, where two distinct clusters mirrored the hyperactivation and immune suppression phenotypes (PMID: 27183822). A discussion of how to think about translating the extensive information from system biology into treatment stratification approaches, or adjunct host-directed therapies, would be helpful.

We agree with the points made and that the two publications above further enhance the paper. We have added discussion of the different disease endpoints on line 65 - 67, the evidence regarding immune herpeactivation versus suppression in the vaccination study on lines 162 - 164, and expanded on the translational implications on lines 349 – 352.

Reviewer #3 (Public review):

Summary:

This perspective article by Reichmann et al. highlights the importance of moving beyond the search for a single, unified immune mechanism to explain host-Mtb interactions. Drawing from studies in immune profiling, host and bacterial genetics, the authors emphasize inconsistencies in the literature and argue for broader, more integrative models. Overall, the article is thought-provoking and well-articulated, raising a concept that is worth further exploration in the TB field.

Strengths:

Timely and relevant in the context of the rapidly expanding multi-omics datasets that provide unprecedented insights into host-Mtb interactions.

Weaknesses (Minor):

Clarity on the notion of a "unified mechanism". It remains unclear whether prior studies explicitly proposed a single unifying immunological model. While inconsistencies in findings exist, they do not necessarily demonstrate that earlier work was uniformly "single-minded". Moreover, heterogeneity in TB has been recognized previously (PMIDs: 19855401, 28736436), which the authors could acknowledge.

We accept this point and have toned down the language, acknowledging that we are expanding on an argument that others have made, whilst focusing on the implications for the systems immunology era, and cite the previous work as suggested.

Evolutionary timeline and industrial-era framing. The evolutionary model is outdated. Ancient DNA studies place the Mtb's most recent common ancestor at ~6,000 years BP (PMIDs: 25141181; 25848958). The Industrial Revolution is cited as a driver of TB expansion, but this remains speculative without bacterial-genomics evidence and should be framed as a hypothesis. Additionally, the claim that Mtb genomes have been conserved only since the Industrial Revolution (lines 165-167) is inaccurate; conservation extends back to the MRCA (PMID: 31448322).

Our understanding is that the evolutionary timeline is not fully resolved, with conflicting evidence proposing different dates. The ancient DNA studies giving a timeline of 6,000 years seem to oppose the evidence of evidence of Mtb infection of humans in the middle east 10,000 years ago, and other estimates suggesting 70,000 years. Therefore, we have cited the work above and added a sentence highlighting that different studies propose different timelines. We would propose the industrial revolution created the ideal societal conditions for the expansion of TB, and this would seem widely accepted in the field, but have added a proviso as suggested. We did not intent to claim that Mtb genomes have been conserved since the industrial revolution, the point we were making is that despite rapid expansion within human populations, it has still remained conserved. We therefore have revised our discussion of the conservation of the Mtb genomes on lines and 72 – 74, 81 – 83 and 185 – 190.

Trained immunity and TB infection. The treatment of trained immunity is incomplete. While BCG vaccination is known to induce trained immunity (ref 59), revaccination does not provide sustained protection (ref 8), and importantly, Mtb infection itself can also impart trained immunity (PMID: 33125891). Including these nuances would strengthen the discussion.

We have refined this section. We did cite PMID: 33125891 in the original submission but have changed the wording to emphasise the point on line …

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Abstract

Line 30: What is an immunological route? Suggest

”...host-pathogen interaction, with diverse immunological processes leading to TB disease (10%) or stable lifelong association or elimination. We suggest these alternate relationships result from the prolonged co-evolution of the pathogen with humans and may even confer a survival advantage in the 90% of exposures that do not progress to disease.”

Thank you, we have reworded the abstract along the lines suggested above, but not identically to allow for other reviewer comments.

Introduction

Ln 43: It is misleading to suggest that the study of TB was the leading influence in establishing the Koch's postulates framework. Many other infections were involved, and Jacob Henle, one of Koch's teachers, is credited with the first clear formulation (see Evans AS. 1976 THE YALE JOURNAL OF BIOLOGY AND MEDICIN PMID: 782050).

We have downplayed the language, stating that TB “contributed” to the formulation if Koch’s postulated.

Ln 46: While the review rightly emphasises intracellular infection in macrophages, the importance and abundance of extracellular bacilli should not be ignored, particularly in transmission and in cavities.

We agree, and have added text on the importance of extracellular bacteria and transmission.

Ln: 56: This is misleading as primary disease prevention is implied, whereas the vaccine was given to individuals presumed to be already infected (TST or IGRA positive). Suggest ..."reduces by 50% progression to overt TB disease when given to those with immunological evidence of latent infection.

Thank you, edit made as suggested

Ln 62: Not sure why it is urgent. Suggest "high priority".

Wording changed as suggested.

Figure 1 needs clarification. The colour scale appears to signify the strength or vigour of the immune response so that disease is associated with high (orange/red) or low (green/blue) activity. The arrows seem to imply either a sequence or a route map when all we really have is an association with a plausible mechanistic link. They might also be taken to imply a hierarchy that is not appropriate. I'm not sure that the X-rays and arrows add anything, and the rectangle provides the key information on its own. Clarify please.

We have clarified the figure legend. We feel the X-rays give the clinical context, and so have kept them, and now state in the legend that this is highlighting that there are diverse pathways leading to active disease to try to emphasise the point the figure is illustrating.

Ln 149-157: I agree that the current dogma is that overt pulmonary disease is required to spread Mtb and fuel disease prevalence. It is vitally important to distinguish the spread of the organism from the occurrence of disease (which does not, of itself, spread). However, both epidemiological (e.g. Ryckman TS, et al. 2022Proc Natl Acad Sci U S A:10.1073/pnas.2211045119) and recent mechanistic (Dinkele R, et al. 2024iScience:10.1016/j.isci.2024.110731, Patterson B, et al. 2024Proc Natl Acad Sci U S A:10. E1073/pnas.2314813121, Warner DF, et al. 2025Nat Rev Microbiol:10.1038/s41579-025-01201-x) studies indicate the importance of asymptomatic infections, and those associated with sputum positivity have recently been recognised by WHO. I think it will be important to acknowledge the importance of this aspect and consider how immune responses may or may not contribute. I regard the view that Mtb is an obligate pathogen, dependent on overt pTB for transmission, as needing to be reviewed.

We agree that we did not give sufficient emphasis to the emerging evidence on asymptomatic infections, and that this may play an important part in transmission in high incidence settings. We now include a discussion on this, and citation of the papers above, on lines 168 – 170.

Ln 159: The terms colonise and colonisation are used, without a clear definition, several times. My view is that both refer to the establishment and replication of an organism on or within a host without associated damage. Where there is associated damage, this is often mediated by immune responses. In this header, I think "establishment in humanity" would be appropriate.

We agree with this point and have changed the header as suggested, and clarified our meaning when we use the term colonisation, which the reviewer correctly interprets.

Ln 181-: I strongly support the view that Mtb has contributed to human selection, even to the suggestion that humanity is adapted to maintain a long-term relationship with Mtb

Thank you, and we have expanded on this evidence as suggested by other reviewers.

Ln 189: improved.

Apologies, typo corrected.

Figure 2: I was also confused by this. The x-axis does not make sense, as a single property should increase. Moreover, does incidence refer to incidence in individuals with that specific balance of resistance and susceptibility, or contribution to overall global incidence - I suspect the latter (also, prevalence would make more sense). At the same time, the legend implies that those with high resistance to colonisation will be infrequent in the population, suggesting that the Y axis should be labelled "frequency in human population". Finally, I can't see what single label could apply to the X axis. While the implication that the majority of global infections reflect a balance between the resistance and susceptibilities is indicated, a frequency distribution does not seem an appropriate representation.

The reviewer is correct that the X axis is aiming to represent two variables, which is not logical, and so we have completely changed this figure to a simple one that we hope makes the point clearly and have amended the legend appropriately. We are aiming to highlight the selective pressures of Mtb on the human population over millennia.

Ln 244: Immunological failure - I agree with the statement but again find the figure (3) unhelpful. Do we start or end in the middle? Is the disease the outside - if so, why are different locations implied? The notion of a maze has some value, but the bacteria should start and finish in the same place by different routes.

We are attempting to illustrate the concept that escape from host immunological control can occur through different mechanisms. As this comment was just from one reviewer, we have left the figure unchanged but have expanded the legend to try to make the point that this is just a conceptual illustration of multiple routes to disease.

Ln 262 onward: I broadly agree with the points made about omic technologies, but would wish to see major emphasis on clear phenotyping of cases. There is something of a contradiction in the review between the emphasis on the multiplicity of immunological processes leading ultimately to disease and the recommendation to analyse via omics, which, in their most widely applied format, bundle these complexities into analyses of the humoral and cellular samples available in blood. Admittedly, the authors point out opportunities for 3-dimensional and single-cell analyses, but it is difficult to see where these end without extrapolation ad infinitum.

We totally agree that clear phenotyping of infection is critical, and expand on this further on lines 307 - 309.

Reviewer #2 (Recommendations for the authors):

I suggest expanding on the genetic determinants of Mtb/host co-evolution.

Thank you, we have now expanded on these sections as suggested.

Reviewer #3 (Recommendations for the authors):

We are in an era of exploding large-scale datasets from multi-omics profiling of Mtb and host interactions, offering an unprecedented lens to understand the complexity of the host immune response to Mtb-a pathogen that has infected human populations for thousands of years. The guiding philosophy for how to interpret this tremendous volume of data and what models can be built from it will be critical. In this context, the perspective article by Reichmann et al. raises an interesting concept: to "avoid unified immune mechanisms" when attempting to understand the immunology underpinning host-Mtb interactions. To support their arguments, the authors review studies and provide evidence from immune profiling, host and bacterial genetics, and showcase several inconsistencies. Overall, this perspective article is well articulated, and the concept is worthwhile for further exploration. A few comments for consideration:

Clarity on the notion of a "unified mechanism". Was there ever a single, clearly proposed unified immunological mechanism? For example, in lines 64-65, the authors criticize that almost all investigations into immune responses to Mtb are based on the premise that a unifying disease mechanism exists. However, after reading the article, it was not clear to me how previous studies attempted to unify the model or what that unifying mechanism was. While inconsistencies in findings certainly exist, they do not necessarily indicate that prior work was guided by a unified framework. I agree that interpreting and exploring data from a broader perspective is valuable, but I am not fully convinced that previous studies were uniformly "single-minded". In fact, the concept of heterogeneity in TB has been previously discussed (e.g., PMIDs: 19855401, 28736436).

We accept this point, and that we have overstated the argument and not acknowledged previous work sufficiently. We now downplay the language and cite the work as proposed.

However, we would propose that essentially all published studies imply that single mechanisms underly development of disease. The authors are not aware of any manuscript that concludes “Therefore, xxxx pathway is one of several that can lead to TB disease”, instead they state “Therefore, xxxx pathway leads to TB disease”. The implication of this language is that the mechanism described occurs in all patients, whilst in fact it likely only is involved in a subset. We have toned down the language and expand on this concept on line 268 – 270.

Evolutionary timeline and industrial-era framing. The evolutionary model needs updating. The manuscript cites a "70,000-year" origin for Mtb, but ancient-DNA studies place the most recent common ancestor at ~6,000 years BP (PMIDs: 25141181; 25848958). The Industrial Revolution is invoked multiple times as a driver of TB expansion, yet the magnitude of its contribution remains debated and, to my knowledge, lacks direct bacterial-genomics evidence for causal attribution; this should be framed as a hypothesis rather than a conclusion. In addition, the statement in lines 165-167 is inaccurate: at the genome level, Mtb has remained highly conserved since its most recent common ancestor-not specifically since the Industrial Revolution (PMID: 31448322).

We accept these points and have made the suggested amendments, as outlined in the public responses. Our understanding is that the evidence about the most common ancestor is controversial; if the divergence of human populations occurred concurrently with Mtb, then this must have been significantly earlier than 6,000 years ago, and so there are conflicting arguments in this domain.

Trained immunity and TB infection. The discussion of trained immunity could be expanded. Reference 59 suggests the induction of innate immune training, but reference 8 reports that revaccination does not confer protection against sustained TB infection, indicating that at least "re"-vaccination may not enhance protection. Furthermore, while BCG is often highlighted as a prototypical inducer of trained immunity, real-world infection occurs through Mtb itself. Importantly, a later study demonstrated that Mtb infection can also impart trained immunity (PMID: 33125891). Integrating these findings would provide a more nuanced view of how both vaccination and infection shape innate immune training in the TB context.

We thank the reviewer for these suggestions and have edited the relevant section to include these studies.

Author response:

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

Public reviews:

Reviewer #1 (Public review):

In this important study, the authors characterized the transformation of neural representations of olfactory stimuli from the primary sensory cortex to multisensory regions in the medial temporal lobe and investigated how they were affected by non-associative learning. The authors used high-density silicon probe recordings from five different cortical regions while familiar vs. novel odors were presented to a head-restrained mouse. This is a timely study because unlike other sensory systems (e.g., vision), the progressive transformation of olfactory information is still poorly understood. The authors report that both odor identity and experience are encoded by all of these five cortical areas but nonetheless some themes emerge. Single neuron tuning of odor identity is broad in the sensory cortices but becomes narrowly tuned in hippocampal regions. Furthermore, while experience affects neuronal response magnitudes in early sensory cortices, it changes the proportion of active neurons in hippocampal regions. Thus, this study is an important step forward in the ongoing quest to understand how olfactory information is progressively transformed along the olfactory pathway.

The study is well-executed. The direct comparison of neuronal representations from five different brain regions is impressive. Conclusions are based on single neuronal level as well as population level decoding analyses. Among all the reported results, one stands out for being remarkably robust. The authors show that the anterior olfactory nucleus (AON), which receives direct input from the olfactory bulb output neurons, was far superior at decoding odor identity as well as novelty compared to all the other brain regions. This is perhaps surprising because the other primary sensory region - the piriform cortex - has been thought to be the canonical site for representing odor identity. A vast majority of studies have focused on aPCx, but direct comparisons between odor coding in the AON and aPCx are rare. The experimental design of this current study allowed the authors to do so and the AON was found to convincingly outperform aPCx. Although this result goes against the canonical model, it is consistent with a few recent studies including one that predicted this outcome based on anatomical and functional comparisons between the AON-projecting tufted cells vs. the aPCx-projecting mitral cells in the olfactory bulb (Chae, Banerjee et. al. 2022). Future experiments are needed to probe the circuit mechanisms that generate this important difference between the two primary olfactory cortices as well as their potential causal roles in odor identification.

The authors were also interested in how familiarity vs. novelty affects neuronal representation across all these brain regions. One weakness of this study is that neuronal responses were not measured during the process of habituation. Neuronal responses were measured after four days of daily exposure to a few odors (familiar) and then some other novel odors were introduced. This creates a confound because the novel vs. familiar stimuli are different odorants and that itself can lead to drastic differences in evoked neural responses. Although the authors try to rule out this confound by doing a clever decoding and Euclidian distance analysis, an alternate more straightforward strategy would have been to measure neuronal activity for each odorant during the process of habituation.

Reviewer #2 (Public review):

This manuscript investigates how olfactory representations are transformed along the cortico-hippocampal pathway in mice during a non-associative learning paradigm involving novel and familiar odors. By recording single-unit activity in several key brain regions (AON, aPCx, LEC, CA1, and SUB), the authors aim to elucidate how stimulus identity and experience are encoded and how these representations change across the pathway.

The study addresses an important question in sensory neuroscience regarding the interplay between sensory processing and signaling novelty/familiarity. It provides insights into how the brain processes and retains sensory experiences, suggesting that the earlier stations in the olfactory pathway, the AON aPCx, play a central role in detecting novelty and encoding odor, while areas deeper into the pathway (LEC, CA1 & Sub) are more sparse and encodes odor identity but not novelty/familiarity. However, there are several concerns related to methodology, data interpretation, and the strength of the conclusions drawn.

Strengths:

The authors combine the use of modern tools to obtain high-density recordings from large populations of neurons at different stages of the olfactory system (although mostly one region at a time) with elegant data analyses to study an important and interesting question.

Weaknesses:

(1) The first and biggest problem I have with this paper is that it is very confusing, and the results seem to be all over the place. In some parts, it seems like the AON and aPCx are more sensitive to novelty; in others, it seems the other way around. I find their metrics confusing and unconvincing. For example, the example cells in Figure 1C show an AON neuron with a very low spontaneous firing rate and a CA1 with a much higher firing rate, but the opposite is true in Figure 2A. So, what are we to make of Figure 2C that shows the difference in firing rates between novel vs. familiar odors measured as a difference in spikes/sec. This seems nearly meaningless. The authors could have used a difference in Z-scored responses to normalize different baseline activity levels. (This is just one example of a problem with the methodology.)

We appreciate the reviewer’s concerns regarding clarity and methodology. It is less clear why all neurons in a given brain area should have similar firing rates. Anatomically defined brain areas typically comprise of multiple cell types, which can have diverse baseline firing rates. Since we computed absolute firing rate differences per neuron (i.e., novel vs. familiar odor responses within the same neuron), baseline differences across neurons do not have a major impact.

The suggestion to use Z-scores instead of absolute firing rate differences is well taken. However, Z-scoring assumes that the underlying data are normally distributed, which is not the case in our dataset. Specifically, when analyzing odor-evoked firing rates on a per-neuron basis, only 4% of neurons exhibit a normal distribution. In cases of skewed distributions, Z-scoring can distort the data by exaggerating small variations, leading to misleading conclusions. We acknowledge that different analysis methods exist, we believe that our chosen approach best reflects the properties of the dataset and avoids potential misinterpretations introduced by inappropriate normalization techniques.

(2) There are a lot of high-level data analyses (e.g., decoding, analyzing decoding errors, calculating mutual information, calculating distances in state space, etc.) but very little neural data (except for Figure 2C, and see my comment above about how this is flawed). So, if responses to novel vs. familiar odors are different in the AON and aPCx, how are they different? Why is decoding accuracy better for novel odors in CA1 but better for familiar odors in SUB (Figure 3A)? The authors identify a small subset of neurons that have unusually high weights in the SVM analyses that contribute to decoding novelty, but they don't tell us which neurons these are and how they are responding differently to novel vs. familiar odors.

We performed additional analyses to address the reviewer’s feedback (Figures 2C-E and lines 118-132) and added more single-neuron data (Figures 1, S3 and S4).

(3) The authors call AON and aPCx "primary sensory cortices" and LEC, CA1, and Sub "multisensory areas". This is a straw man argument. For example, we now know that PCx encodes multimodal signals (Poo et al. 2021, Federman et al., 2024; Kehl et al., 2024), and LEC receives direct OB inputs, which has traditionally been the criterion for being considered a "primary olfactory cortical area". So, this terminology is outdated and wrong, and although it suits the authors' needs here in drawing distinctions, it is simplistic and not helpful moving forward.

We appreciate the reviewer’s concern regarding the classification of brain regions as “primary sensory” versus “multisensory.” Of note, the cited studies (Poo et al., 2021; Federman et al., 2024; Kehl et al., 2024) focus on posterior PCx (pPCx), while our recordings were conducted in very anterior section of anterior PCx. The aPCx and pPCx have distinct patterns of connectivity, both anatomically and functionally. To the best of our knowledge, there is no evidence for multimodal responses in aPCx, whereas there is for LEC, CA1 and SUB. Furthermore, our distinction is not based on a connectivity argument, as the reviewer suggests, but on differences in the α-Poisson ratio (Figure 1E and F).

To avoid confusion due to definitions of what constitutes a “primary sensory” region, we adopted a more neutral description throughout the manuscript.

(4) Why not simply report z-scored firing rates for all neurons as a function of trial number? (e.g., Jacobson & Friedrich, 2018). Figure 2C is not sufficient.

Regarding z-scores, please see response to 1). We further added a figure showing responses of all neurons to novel stimuli (using ROC instead of z-scoring, as described previously (e.g. Cohen et al. Nature 2012). We added the following figure to the supplementary for the completeness of the analysis (S2E).

For example, in the Discussion, they say, "novel stimuli caused larger increases in firing rates than familiar stimuli" (L. 270), but what does this mean?

This means that on average, the population of neurons exhibit higher firing rates in response to novel odors compared to familiar ones.

Odors typically increase the firing in some neurons and suppress firing in others. Where does the delta come from? Is this because novel odors more strongly activate neurons that increase their firing or because familiar odors more strongly suppress neurons?

We thank the reviewer for this valuable feedback and extended the characterization of firing rate properties, including a separate analysis of neurons i) significantly excited by odorants, ii) significantly inhibited by odorants and iii) not responsive to odorants. We added the analysis and corresponding discussion to the main manuscript (Figures 2C-E and lines 118-132)

(5) Lines 122-124 - If cells in AON and aPCx responded the same way to novel and familiar odors, then we would say that they only encode for odor and not at all for experience. So, I don't understand why the authors say these areas code for a "mixed representation of chemical identity and experience." "On the other hand," if LEC, CA1, and SUB are odor selective and only encode novel odors, then these areas, not AON and aPCx, are the jointly encoding chemical identity and experience. Also, I do not understand why, here, they say that AON and PCx respond to both while LEC, CA1, and SUB were selective for novel stimuli, but the authors then go on to argue that novelty is encoded in the AON and PCx, but not in the LEC, CA1, and SUB.

We appreciate the reviewer’s request for clarification. Throughout the brain areas we studied, odorant identity and experience can be decoded. However, the way information is represented is different between regions. We acknowledge that that “mixed” representation is a misleading term and removed it from the manuscript.

In AON and aPCx, neurons significantly respond to both novel and familiar odors. However, the magnitude of their responses to novel and familiar odors is sufficiently distinct to allow for decoding of odor experience (i.e., whether an odor is novel or familiar). Moreover, novelty engages more neurons in encoding the stimulus (Figure 2D). In neural space, the position of an odor’s representation in AON and aPCx shifts depending on whether it is novel or familiar, meaning that experience modifies the neural representation of odor identity. This suggests that in these regions the two representations are intertwined.

In contrast, some neurons in LEC, CA1, and SUB exhibit responses to novel odors, but few neurons respond to familiar odors at all. This suggests a more selective encoding of novelty.

(6) Lines 132-140 - As presented in the text and the figure, this section is poorly written and confusing. Their use of the word "shuffled" is a major source of this confusion, because this typically is the control that produces outcomes at the chance level. More importantly, they did the wrong analysis here. The better and, I think, the only way to do this analysis correctly is to train on some of the odors and test on an untrained odor (i.e., what Bernardi et al., 2021 called "cross-condition generalization performance"; CCGP).

We appreciate the feedback and thank the reviewer for the recommendation to implement cross-condition generalization performance (CCGP) as used in Bernardi et al., 2020. We acknowledge that the term "shuffled" may have caused confusion, as it typically refers to control analyses producing chance-level outcomes. In our case, by "shuffling" we shuffled the identity of novel and familiar odors to assess how much the decoder relies on odor identity when distinguishing novelty. This test provided insight into how novelty-based structure exists within neural activity beyond random grouping but does not directly assess generalization.

As suggested, we used CCGP to measure how well novelty-related representations generalize across different odors. Our findings show that in AON and aPCx, novelty-related information is indeed highly generalizable, supporting the idea that these regions encode novelty in a less odor-selective manner (Figure 2K).

Reviewer #3 (Public review):

In this manuscript, the authors investigate how odor-evoked neural activity is modulated by experience within the olfactory-hippocampal network. The authors perform extracellular recordings in the anterior olfactory nucleus (AON), the anterior piriform (aPCx) and lateral entorhinal cortex (LEC), the hippocampus (CA1), and the subiculum (SUB), in naïve mice and in mice repeatedly exposed to the same odorants. They determine the response properties of individual neurons and use population decoding analyses to assess the effect of experience on odor information coding across these regions.

The authors' findings show that odor identity is represented in all recorded areas, but that the response magnitude and selectivity of neurons are differentially modulated by experience across the olfactory-hippocampal pathway.

Overall, this work represents a valuable multi-region data set of odor-evoked neural activity. However, limitations in the interpretability of odor experience of the behavioral paradigm, and limitations in experimental design and analysis, restrict the conclusions that can be drawn from this study.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Some suggestions, in no particular order, to further improve the manuscript:

(1) The example neuronal responses for CA1 and SUB in Figure 1 are not very inspiring. To my eyes, the odor period response is not that different from the baseline period. In general, a thorough characterization of firing rate properties during the odor period between the different brain regions would be informative.

We thank the reviewer for this valuable feedback. We have replaced the example neurons from CA1 and SUB in Figure 1C. We further extended the characterization of firing rate properties, including a separate analysis of neurons i) significantly excited by odorants, ii) significantly inhibited by odorants and iii) not responsive to odorants. We added the analysis and corresponding discussion to the main manuscript (Figures 2C-E and lines 118-132)

(2) For the summary in Figure 1, why not show neuronal responses as z-scored firing rates as opposed to auROC?

We chose to use auROC instead of z-scored firing rates due to the non-normality of the dataset, which can distort results when using z-scores. Specifically, z-scoring can exaggerate small deviations in neurons with low responsiveness, potentially leading to misleading conclusions. auROC provides a more robust measure of response change that is less sensitive to these distortions because it does not assume any specific distribution. This approach has been used previously (e.g. Cohen et al. 2012, Nature).

(3) To study novelty, the authors presented odorants that were not used during four days of habituation. But this design makes it hard to dissociate odor identity from novelty. Why not track the response of the same odorants during the habituation process itself?

We respectfully disagree with the argument that using different stimuli as novel and familiar constitutes a confound in our analysis. In our study, we used multiple different, structurally dissimilar single molecule chemicals which were randomly assigned to novel and familiar categories in each animal. If individual stimuli did cause “drastic differences in evoked neural responses”, these would be evenly distributed between novel and familiar stimuli. It is therefore extremely unlikely that the clear differences we observed between novel and familiar conditions and between brain areas can be attributed to the contribution of individual stimuli, in particular given our analyses was performed at the population level. In fact, we observed that responses between novel and familiar conditions were qualitatively very similar in the short time window after odor onset (Figure 1G and H).

Importantly, the goal of this study was to investigate the impact of long-term habituation over more than 4 days, rather than short term habituation during one behavioral session. However, tracking the activity of large numbers of neurons across multiple days presents a significant technical challenge, due to the difficulty of identifying stable single-unit recordings over extended periods of time with sufficient certainty. Tools that facilitate tracking have recently been developed (e.g. Yuan AX et al., Elife. 2024) and it will be interesting to apply them to our dataset in the future.

(4) Since novel odors lead to greater sniffing and sniffing strongly influences firing rates in the olfactory system, the authors decided to focus on a 400 ms window with similar sniffing rates for both novel vs. familiar odors. Although I understand the rationale for this choice, I worry that this is too restrictive, and it may not capture the full extent of the phenomenology.

Could the authors model the effect of sniffing on firing rates of individual neurons from the data, and then check whether the odor response for novel context can be fully explained just by increased sniffing or not?

It is an interesting suggestion to extend the window of analysis and observe how responses evolve with sniffing (and other behavioral reactions). To address this, we added an additional figure to the supplementary material, showing the mean responses of all neurons to novel stimuli during the entire odor presentation window (Fig. S1B).

As suggested, we further created a Generalized Linear Model (GLM) for the entire 2s odor stimulation period, incorporating sniffing and novelty as independent variables. As expected, sniffing had a dominant impact on firing rate in all brain areas. A smaller proportion of neurons was modulated by novelty or by the interaction between novelty x breathing, suggesting the entrainment of neural activity by sniffing during the response to novel odors. These results support our decision to focus the analysis on the early 400ms window in order to dissociate the effects of novelty and behavioral responses. Taken together, our results suggest that odorant responses are modulated by novelty early during odorant processing, whereas at later stages sniffing becomes the predominant factor driving firing (Figure S2C-D).

(5) The authors conclude that aPCx has a subset of neurons dedicated to familiar odors based on the distribution of SVM weights in Figure 3D. To me, this is the weakest conclusion of the paper because although significant, the effect size is paltry; the central tendencies are hardly different for the two conditions in aPCx. Could the authors show the PSTHs of some of these neurons to make this point more convincing?

We appreciate the reviewer’s concern regarding the effect size. To strengthen our conclusion, we now include PSTHs of representative neurons in the least 10% and best 10% of neuronal population based on the SVM analysis (Figures S3 and S4). We hope this provides more clarity and support for the interpretation that there is a subset of neurons in aPCx that show greater sensitivity to familiar odors, despite the relatively modest central tendency differences.

In the revised manuscript, we discuss the effect size more explicitly in the text to provide context for its significance (lines 193 - 195).

Reviewer #2 (Recommendations for the authors):

(1) The authors only talk about "responsive" neurons. Does this include neurons whose activity increases significantly (activated) and neurons whose activity decreases (suppressed)?

Yes, the term "responsive" refers to neurons whose activity either increases significantly (excited) or decreases (inhibited) in response to the odor stimuli. We performed additional analyses to characterize responses separately for the different groups (Figure 2C-E and lines 118-132).

(2) Line 54 - The Schoonover paper doesn't show that cells lose their responses to odors, but rather that the population of cells that respond to odors changes with time. That is, population responses don't become more sparse

The fact that “the population of cells that respond to odors changes with time”, implies that some neurons lose their responsiveness (e.g. unit 2 in Figure 1 of Schoonover et al., 2021), while others become responsive (e.g. unit 1 in Figure 1 of Schoonover et al., 2021). Frequent responses reduce drift rate (Figure 4 of Schoonover et al., 2021), thus fewer neurons loose or gain responsiveness. We have revised the manuscript to clarify this.

(3) Line 104 - "Recurrent" is incorrectly used here. I think the authors mean "repeated" or something more like that.

Thank you for pointing this out. We replaced "recurrent" with "repeated".

(4) Figure 3D - What is the scale bar here?

We apologize for the accidental omission. The scale bar was be added to Figure 3D in the revised version of the manuscript.

(5) Line 377 - They say they lowered their electrodes to "200 um/s per second." This must be incorrect. Is this just a typo, or is it really 200 um/s, because that's really fast?

Thank you for pointing this out. It was 20 to 60 um/s, the change has been made in the manuscript.

(6) Line 431: The authors say they used auROC to calculate changes in firing rates (which I think is only shown in Figure 1D). Note that auROC measures the discriminability of two distributions, not the strength or change in the strength of response.

Indeed we used auROC to measure the discriminability of firing between baseline and during stimulus response. We have corrected the wording in the methods.

(7) Figure 1B: The anatomical locations of the five areas they recorded from are straightforward, and this figure is not hugely helpful. However, the reader would benefit tremendously by including an experimental schematic. As is, we needed to scour the text and methods sections to understand exactly what they did when.

We thank the reviewer for this suggestion. We included an experimental schematic in the supplementary material.

(8) Figure 1F(left): This plot is much less useful without showing a pre-odor window, even if only times after the odor onset were used for calculation alpha

We appreciate this concern, however the goal of Figure 1F is to illustrate the meaning of the alpha value itself. We chose not to include a pre-odor window comparison to avoid confusing the reader.

(9) Figure 2A: What are the bar plots above the raster plots? Are these firing rates? Are the bars overlaid or stacked? Where is the y-axis scale bar?

The bar plots above the raster plots represent a histogram of the spike count/trials over time, with a bin width of 50 ms. These bars are overlaid on the raster plot. We will include a y-axis scale bar in the revised figure to clarify the presentation.

(10) Figure 4G: This makes no sense. First, the Y axis is supposed to measure standard deviation, but the axis label is spikes/s. Second, if responses in the AON are much less reliable than responses in "deeper" areas, why is odor decoding in AON so much better than in the other areas?

We acknowledge the error in the axis label, and we will correct it to indicate the correct units. AON has a larger response variability but also larger responses magnitudes, which can explain the higher decoding accuracy.

(11) From the model and text, one predicts that the lifetime sparseness increases along the pathway. The authors should use this metric as well/instead of "odor selectivity" because of problems with arbitrary thresholding.

We acknowledge that lifetime sparseness, often computed using lifetime kurtosis, can be an informative measure of selectivity. However, we believe it has limitations that make it less suitable for our analysis. One key issue is that lifetime sparseness does not account for the stability of responses across multiple presentations of the same stimulus. In contrast, our odor selectivity measure incorporates trial-to-trial variability by considering responses over 10 trials and assessing significance using a Wilcoxon test compared to baseline. While the choice of a p-value threshold (e.g., 0.05) is somewhat arbitrary, it is a widely accepted statistical convention. Additionally, lifetime sparseness does not account for excitatory and inhibitory responses. For example, if a neuron X is strongly inhibited by odor A, strongly excited by odor B, and unresponsive to odors C and D, lifetime sparseness would classify it as highly selective for odor B, without capturing its inhibitory selectivity for odor A. The lifetime sparseness will be higher than if X was simply unresponsive for A.

Our odor selectivity measure addresses this by considering both excitation and inhibition as potential responses. Thus, while lifetime sparseness could provide a useful complementary perspective in another type of dataset, it does not fully capture the dynamics of odor selectivity here.

Author response 1.

Lifetime Kurtosis distribution per region.

Reviewer #3 (Recommendations for the authors):

Main points:

(1) The authors use a non-associative learning paradigm - repeated odor exposure - to test how experience modulates odor responses along the olfactory-hippocampal pathway. While repeated odor exposure clearly modulates odor-evoked neural activity, the relevance of this modulation and its differential effect across different brain areas are difficult to assess in the absence of any behavioral read-outs.

Our experimental paradigm involves a robust, reliable behavioral readout of non-associative learning. Novel olfactory stimuli evoke a well-characterized orienting reaction, which includes a multitude of physiological reactions, including exploratory sniffing, facial movements and pupil dilation (Modirshanechi et al., Trends Neuroscience 2023). In our study, we focused on exploration sniffing.

Compared to associative learning, non-associative learning might have received less attention. However, it is critically important because it forms the foundation for how organisms adapt to their environment through experience without forming associations. This is highlighted by the fact that non-instrumental stimuli can be remembered in large number (Standing, 1973) and with remarkable detail (Brady et al., 2008). While non-associative learning can thus create vast, implicit memory of stimuli in the environment, it is unclear how stimulus representations reflect this memory. Our study contributes to answering this question. We describe the impact of experience on olfactory sensory representations and reveal a transformation of representations from olfactory cortical to hippocampal structures. Our findings also indicate that sensory responses to familiar stimuli persist within sensory cortical and hippocampal regions, even after spontaneous orienting behaviors habituated. Further studies involving experimental manipulation techniques are needed to elucidate the causal mechanisms underlying the formation of stimulus memory during non-associative learning.

(2) The authors discuss the olfactory-hippocampal pathway as a transition from primary sensory (AON, aPCx) to associative areas (LEC, CA1, SUB). While this is reasonable, given the known circuit connectivity, other interpretations are possible. For example, AON, aPCx, and LEC receive direct inputs from the olfactory bulb ('primary cortex'), while CA1 and SUB do not; AON receives direct top-down inputs from CA1 ('associative cortex'), while aPCx does not. In fact, the data presented in this manuscript does not appear to support a consistent, smooth transformation from sensory to associative, as implied by the authors (e.g. Figure 4A, F, and G).

Thank you for this insightful comment. Indeed, there are complexities in the circuitry, and the relationships between different areas are not linear. We believe that AON and aPCx are distinctly different from LEC, CA1 and SUB, as the latter areas have been shown to integrate multimodal sensory information. To avoid confusion due to definitions of what constitutes a “primary sensory” region, we adopted a more neutral description throughout the manuscript. We also removed the term “gradual” to describe the transition of neural representations from olfactory cortical to hippocampal areas.

(3) The analysis of odor-evoked responses is focused on a 400 ms window to exclude differences in sniffing behavior. This window spans 200 ms before and after the first inhalation after odor onset. Inhalation onset initiates neural odor responses - why do the authors include neural data before inhalation onset?

The reason to include a brief time window prior to odor onset is to account for what is often called “partical” sniffs. In our experimental setup, odor delivery is not triggered by the animal’s inhalation. Therefore, it can happen that an animal has just begun to inhale when the stimulus is delivered. In this case, the animal is exposed to odorant molecules prior to the first complete inhalation after odor onset. We acknowledge that this limits the temporal resolution of our measurements, but it does not affect the comparison of sensory representations between different brain areas.

It would also be interesting to explore the effect of sniffing behavior (see point 2) on odor-evoked neural activity.

Thank you for your comment, we performed additional analysis including a GLM to address this question (Figure S2C-D).

Minor points:

(4) Figure 2A represents raster plots for 2 neurons per area - it is unclear how to distinguish between the 2 neurons in the plots.

Figure 2A shows one example neuron per brain area. Each neurons has two raster plot which indicate responses to either a novel (orange) or a familiar stimulus (blue). We have revised the figure caption for clarity.

(5) Overall, axes should be kept consistent and labeled in more detail. For example, Figure 2H and I are difficult to compare, given that the y-axis changes and that decoding accuracies are difficult to estimate without additional marks on the y-axis.

Axes are indeed different, because chance level decoding accuracy is different between those two figures. The decoding between novel and familiar odors has a chance level of 0.5, while chance level decoding odors is 0.1 (there are 10 odors to decode the identity from).

(6) Some parts of the discussion seem only loosely related to the data presented in this manuscript. For example, the statement that 'AON rather than aPCx should be considered as the primary sensory cortex in olfaction' seems out of context. Similarly, it would be helpful to provide data on the stability of subpopulations of neurons tuned to familiar odors, rather than simply speculate that they could be stable. The authors could summarize more speculative statements in an 'Ideas and Speculation' subsection.

Thank you for your comment. We appreciate your perspective on our hypotheses. We have revised the discussion accordingly. Specifically, we removed the discussion of stable subpopulations, since we have not performed longitudinal tracking in this study.

(7) The authors should try to reference relevant published work more comprehensively.

Thank you for your comment. We attempted to include relevant published work without exceeding the limit for references but might have overseen important contributions. We apologize to our colleagues, whose relevant work might not have been cited.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The main contributions of this paper are: (1) a replication of the surprising prior finding that information about peripherally-presented stimuli can be decoded from foveal V1 (Williams et al 2008), (2) a new demonstration of cross-decoding between stimuli presented in the periphery and stimuli presented at the fovea, (3) a demonstration that the information present in the fovea is based on shape not semantic category, and (4) a demonstration that the strength of foveal information about peripheral targets is correlated with the univariate response in the same block in IPS.

Strengths:

The design and methods appear sound, and finding (2) above is new, and importantly constrains our understanding of this surprising phenomenon. The basic effect investigated here is so surprising that even though it has been replicated several times since it was first reported in 2008, it is useful to replicate it again.

We thank the reviewer for their summary. While we agree with many points, we would like to respectfully push back on the notion that this work is a replication of Williams et al. (2008). What our findings share with those of Williams is a report of surprising decoding at the fovea without foveal stimulation. Beyond this similarity, we treat these as related but clearly separate findings, for the following reasons:

(1) Foveal feedback, as shown by Williams et al. (2008) and others during fixation, was only observed during a shape discrimination task, specific to the presented stimulus. Control experiments without such a task (or a color-related task) did not show effects of foveal feedback. In contrast, in the present study, the participants’ task was merely to perform saccades towards stimuli, independently of target features. We thus show that foveal feedback can occur independently of a task related to stimulus features. This dissociation demonstrates that our study must be tapping into something different than reported by Williams.

(2) In a related study, Kroell and Rolfs (2022, 2025) demonstrated a connection between foveal feedback and saccade preparation, including the temporal details of the onset of this effect before saccade execution, highlighting the close link of this effect to saccade preparation. Here we used a very similar behavioral task to capture this saccade-related effect in neural recordings and investigate how early it occurs and what its nature is. Thus, there is a clear motivation for this study in the context of eye movement preparation that is separate from the previous work by Williams.

(3) Lastly, decoding in the experimental task was positively associated with activity in FEF and IPS, areas that have been reliably linked to saccade preparation. We have now also performed an additional analysis (see our response to Specific point 2 of Reviewer 2) showing that decoding in the control condition did not show the same association, further supporting the link of foveal feedback to saccade preparation. 

Despite our emphasis on these critical differences in studies, covert peripheral attention, as required by the task in Williams et al., and saccade preparation in natural vision, as in our study, are tightly coupled processes. Indeed, the task in Williams et al. would, during natural vision, likely involve an eye movement to the peripheral target. While speculative, a parsimonious and ecologically valid explanation is that both ours and earlier studies involve eye movement preparation, for which execution is suppressed, however, in studies enforcing fixation (e.g., Williams et al., 2008). We now discuss this idea of a shared underlying mechanism more extensively in the revised manuscript (pg 8 ln 228-240). 

Weaknesses:

(1) The paper, including in the title ("Feedback of peripheral saccade targets to early foveal cortex") seems to assume that the feedback to foveal cortex occurs in conjunction with saccade preparation. However, participants in the original Williams et al (2008) paper never made saccades to the peripheral stimuli. So, saccade preparation is not necessary for this effect to occur. Some acknowledgement and discussion of this prior evidence against the interpretation of the effect as due to saccade preparation would be useful. (e.g., one might argue that saccade preparation is automatic when attending to peripheral stimuli.)

We agree that the effects Williams et al. showed were not sufficiently discussed in the first version of this manuscript. To more clearly engage with these findings we now introduce saccade related foveal feedback (foveal prediction) and foveal feedback during fixation separately in the introduction (pg 2 ln 46-59).

We further added another section in the discussion called “Foveal feedback during saccade preparation” in which we discuss how our findings are related to Williams et al. and how they differ (pg 8 ln 211-240). 

As described in our previous response, we believe that our findings go beyond those described by Williams et al. (2008) and others in significant ways. However, during natural vision, the paradigm used by Williams et al. (2008) would likely be solved using an eye movement. Thus, while participants in Williams et al. (2008) did not execute saccades, it appears plausible that they have prepared saccades. Given the fact that covert peripheral attention and saccade preparation are tightly coupled processes (Kowler et al., 1995, Vis Res; Deubel & Schneider, 1996, Vis Res; Montagnini & Castet, 2007, J Vis; Rolfs & Carrasco, 2012, J Neurosci; Rolfs et al., 2011, Nat Neurosci), their results are parsimoniously explained by saccade preparation (but not execution) to a behaviorally relevant target.

(2) The most important new finding from this paper is the cross-decodability between stimuli presented in the fovea and stimuli presented in the periphery. This finding should be related to the prior behavioral finding (Yu & Shim, 2016) that when a foveal foil stimulus identical to a peripheral target is presented 150 ms after the onset of the peripheral target, visual discrimination of the peripheral target is improved, and this congruency effect occurred even though participants did not consciously perceive the foveal stimulus (Yu, Q., & Shim, W. M., 2016). Modulating foveal representation can influence visual discrimination in the periphery (Journal of Vision, 16(3), 15-15).

We thank the reviewer for highlighting this highly relevant reference. In the revised version of the manuscript, we now put more emphasis on the finding of cross-decodability (pg 2 ln 60-61). We now also discuss Yu et al.’s finding, which support our conclusion that foveal feedback and direct stimulus presentation share representational formats in early visual areas (pg 9 ln 277-279).

(3) The prior literature should be laid out more clearly. For example, most readers will not realize that the basic effect of decodability of peripherally-presented stimuli in the fovea was first reported in 2008, and that that original paper already showed that the effect cannot arise from spillover effects from peripheral retinotopic cortex because it was not present in a retinotopic location between the cortical locus corresponding to the peripheral target and the fovea. (For example, this claim on lines 56-57 is not correct: "it remains unknown 1) whether information is fed back all the way to early visual areas".) What is needed is a clear presentation of the prior findings in one place in the introduction to the paper, followed by an articulation and motivation of the new questions addressed in this paper. If I were writing the paper, I would focus on the cross-decodability between foveal and peripheral stimuli, as I think that is the most revealing finding.

We agree that the structure of the introduction did not sufficiently place our work in the context of prior literature. We have now expanded upon our Introduction section to discuss past studies of saccade- and fixation-related foveal feedback (pg 2 ln 49-59), laying out how this effect has been studied previously. We also removed the claim that "it remains unknown 1) whether information is fed back all the way to early visual areas", where our intention was to specifically focus on foveal prediction. We realize that this was not clear and hence removed this section. Instead, we now place a stronger focus on the cross-decodability finding (pg 2 ln 60-61).

Reviewer #2 (Public review):

Summary:

This study investigated whether the identity of a peripheral saccade target object is predictively fed back to the foveal retinotopic cortex during saccade preparation, a critical prediction of the foveal prediction hypothesis proposed by Kroell & Rolfs (2022). To achieve this, the authors leveraged a gaze-contingent fMRI paradigm, where the peripheral saccade target was removed before the eyes landed near it, and used multivariate decoding analysis to quantify identity information in the foveal cortex. The results showed that the identity of the saccade target object can be decoded based on foveal cortex activity, despite the fovea never directly viewing the object, and that the foveal feedback representation was similar to passive viewing and not explained by spillover effects. Additionally, exploratory analysis suggested IPS as a candidate region mediating such foveal decodability. Overall, these findings provide neural evidence for the foveal cortex processing the features of the saccade target object, potentially supporting the maintenance of perceptual stability across saccadic eye movements.

Strengths:

This study is well-motivated by previous theoretical findings (Kroell & Rolfs, 2022), aiming to provide neural evidence for a potential neural mechanism of trans-saccadic perceptual stability. The question is important, and the gaze-contingent fMRI paradigm is a solid methodological choice for the research goal. The use of stimuli allowing orthogonal decoding of stimulus category vs stimulus shape is a nice strength, and the resulting distinctions in decoded information by brain region are clean. The results will be of interest to readers in the field, and they fill in some untested questions regarding pre-saccadic remapping and foveal feedback.

We thank the reviewer for the positive assessment of our study.

Weaknesses:

The conclusions feel a bit over-reaching; some strong theoretical claims are not fully supported, and the framing of prior literature is currently too narrow. A critical weakness lies in the inability to test a distinction between these findings (claiming to demonstrate that "feedback during saccade preparation must underlie this effect") and foveal feedback previously found during passive fixation (Williams et al., 2008). Discussions (and perhaps control analysis/experiments) about how these findings are specific to the saccade target and the temporal constraints on these effects are lacking. The relationship between the concepts of foveal prediction, foveal feedback, and predictive remapping needs more thorough treatment. The choice to use only 4 stimuli is justified in the manuscript, but remains an important limitation. The IPS results are intriguing but could be strengthened by additional control analysis. Finally, the manuscript claims the study was pre-registered ("detailing the hypotheses, methodology, and planned analyses prior to data collection"), but on the OSF link provided, there is just a brief summary paragraph, and the website says "there have been no completed registrations of this project".

We thank the reviewer for these helpful considerations. We agree that some of the claims were not sufficiently supported by the evidence, and in the revised manuscript, we added nuance to those claims (pg 8 ln 211-240). Furthermore, we now address more directly the distinction between foveal feedback during fixation and foveal feedback (foveal prediction) during saccade preparation. In particular, we now describe the literature about these two effects separately in the introduction (pg 2 ln 46-59), and we have added a new section in the discussion (“Foveal feedback during saccade preparation”) that more thoroughly explains why a passive fixation condition would have been unlikely to produce the same results we find (pg 8 ln 211-227). We also adapted the section about “Saccadic remapping or foveal prediction”, clearly delineating foveal prediction from feature remapping and predictive updating of attention pointers. As recommended by the reviewer, we conducted the parametric modulation analyses on the control condition, strengthening the claim that our findings are saccade-related. These results were added as Supplementary Figure 2 and are discussed in (pg 7 ln 190-191) and (pg 8 ln 224-227). 

Lastly, we would like to apologize about a mistake we made with the pre-registration. We realized that the pre-registration had indeed not been submitted. We have now done so without changing the pre-registration itself, which can be seen from the recent activity of the preregistration (screenshot attached in the end). After consulting an open science expert at the University of Leipzig, we added a note of this mistake to the methods section of the revised manuscript (pg 10 ln 326-332). We could remove reference to this preregistration altogether, but would keep it at the discretion of the editor. 

Specifics:

(1) In the eccentricity-dependent decoding results (Figure 2B), are there any statistical tests to support the results being a U-shaped curve? The dip isn't especially pronounced. Is 4 degrees lower than the further ones? Are there alternative methods of quantifying this (e.g., fitting it to a linear and quadratic function)?

We statistically tested the U-shaped relationship using a weighted quadratic regression, which showed significant positive curvature for decoding between fovea and periphery in all early visual areas (V1: t(27) = 3.98, p = 0.008, V2: t(27) = 3.03, p = 0.02, V3: t(27)= 2.776, p = 0.025, one-sided). We now report these results in the revised manuscript (pg 5 ln 137-138).

(2) In the parametric modulation analysis, the evidence for IPS being the only region showing stronger fovea vs peripheral beta values was weak, especially given the exploratory nature of this analysis. The raw beta value can reflect other things, such as global brain fluctuations or signal-to-noise ratio. I would also want to see the results of the same analysis performed on the control condition decoding results.

We appreciate the reviewer’s suggestion and repeated the same parametric modulation analysis on the control condition to assess the influence of potential confounds on the overall beta values (Supplementary Figure 2). The results show a negative association between foveal decoding and FEF and IPS (likely because eye movements in the control condition lead to less foveal presentation of the stimulus) and a positive association with LO. Peripheral decoding was not associated with significant changes in any of the ROIs, indicating that global brain fluctuations alone are not responsible for the effects reported in the experimental condition. The results of this analysis thus show a specific positive association of IPS activity with the experimental condition, not the control condition, which is in line with the idea that the foveal feedback effect reported in this study may be related to saccade preparation.

(3) Many of the claims feel overstated. There is an emphasis throughout the manuscript (including claims in the abstract) that these findings demonstrate foveal prediction, specifically that "image-specific feedback during saccade preparation must underlie this effect." To my understanding, one of the key aspects of the foveal prediction phenomenon that ties it closely to trans-saccadic stability is its specificity to the saccade target but not to other objects in the environment. However, it is not clear to what degree the observed findings are specific to saccade preparation and the peripheral saccade target. Should the observers be asked to make a saccade to another fixation location, or simply maintain passive fixation, will foveal retinotopic cortex similarly contain the object's identity information? Without these control conditions, the results are consistent with foveal prediction, but do not definitively demonstrate that as the cause, so claims need to be toned down.

We fully agree with the reviewer and toned down claims about foveal prediction. We engage with the questions raised by the reviewer more thoroughly in the new discussion section “Foveal feedback during saccade preparation”.

In addition, we agree that another condition in which subjects make a saccade towards a different location would have been a great addition that we also considered, but due to concerns with statistical power did not add. While including such a condition exceeds the scope of the current study, we included this limitation in the Discussion section (pg 10 ln 316) and hope that future studies will address this question.

(4) Another critical aspect is the temporal locus of the feedback signal. In the paradigm, the authors ensured that the saccade target object was never foveated via the gaze-contingent procedure and a conservative data exclusion criterion, thus enabling the test of feedback signals to foveal retinotopic cortex. However, due to the temporal sluggishness of fMRI BOLD signals, it is unclear when the feedback signal arrives at the foveal retinotopic cortex. In other words, it is possible that the feedback signal arrives after the eyes land at the saccade target location. This possibility is also bolstered by Chambers et al. (2013)'s TMS study, where they found that TMS to the foveal cortex at 350-400 ms SOA interrupts the peripheral discrimination task. The authors should qualify their claims of the results occurring "during saccade preparation" (e.g., pg 1 ln 22) throughout the manuscript, and discuss the importance of temporal dynamics of the effect in supporting stability across saccades.

We fully agree that the sluggishness of the fMRI signal presents an important challenge in investigating foveal feedback. We have now included this limitation in the discussion (pg 10 ln 306-318). We also clarify that our argument connects to previous studies investigating the temporal dynamics of foveal feedback using similar tasks (pg 10 ln 313-316). Specifically, in their psychophysical work, Kroell and Rolfs (2022) and (2025) showed that foveal feedback occurs before saccade execution with a peak around 80 ms before the eye movement. 

(5) Relatedly, the claims that result in this paradigm reflect "activity exclusively related to predictive feedback" and "must originate from predictive rather than direct visual processes" (e.g., lines 60-65 and throughout) need to be toned down. The experimental design nicely rules out direct visual foveal stimulation, but predictive feedback is not the only alternative to that. The activation could also reflect mental imagery, visual working memory, attention, etc. Importantly, the experiment uses a block design, where the same exact image is presented multiple times over the block, and the activation is taken for the block as a whole. Thus, while at no point was the image presented at the fovea, there could still be more going on than temporally-specific and saccade-specific predictive feedback.

We agree that those claims could have misled the reader. Our intention was to state that the activation originates from feedback rather than direct foveal stimulation because of the nature of the design. We have now clarified these statements (pg 2 ln 65) and also included a discussion of other effects including imagery and working memory in the limitations section (pg 10 ln 306-313).

(6) The authors should avoid using the terms foveal feedback and foveal prediction interchangeably. To me, foveal feedback refers to the findings of Williams et al. (2008), where participants maintained passive fixation and discriminated objects in the periphery (see also Fan et al., 2016), whereas foveal prediction refers to the neural mechanism hypothesized by Kroell & Rolfs (2022), occurring before a saccade to the target object and contains task irrelevant feature information.

We agree, and we have now adopted a clearer distinction between these terms, referring to foveal prediction only when discussing the distinct predictive nature of the effect discovered by Kroell and Rolfs (2022). Otherwise we referred to this effect as foveal feedback.

(7) More broadly, the treatment of how foveal prediction relates to saccadic remapping is overly simplistic. The authors seem to be taking the perspective that remapping is an attentional phenomenon marked by remapping of only attentional/spatial pointers, but this is not the classic or widely accepted definition of remapping. Within the field of saccadic remapping, it is an ongoing debate whether (/how/where/when) information about stimulus content is remapped alongside spatial location (and also whether the attentional pointer concept is even neurophysiologically viable). This relationship between saccadic remapping and foveal prediction needs clarification and deeper treatment, in both the introduction and discussion.

We thank the reviewer for their remarks. We reformulated the discussion section on “Saccadic remapping or foveal prediction” to include the nuances about spatial and feature remapping laid out in the reviewer’s comment (pg 8-9 ln 241-269). We also put a stronger focus on the special role the fovea seems to be playing regarding the feedback of visual features (pg 8-9 ln 265-269).

(8) As part of this enhanced discussion, the findings should be better integrated with prior studies. E.g., there is some evidence for predictive remapping inducing integration of non-spatial features (some by the authors themselves; Harrison et al., 2013; Szinte et al., 2015). How do these findings relate to the observed results? Can the results simply be a special case of non-spatial feature integration between the currently attended and remapped location (fovea)? How are the results different from neurophysiological evidence for facilitation of the saccade target object's feature across the visual field (Burrow et al., 2014)? How might the results be reconciled with a prior fMRI study that failed to find decoding of stimulus content in remapped responses (Lescroart et al, 2016)? Might this reflect a difference between peripheral-to-peripheral vs peripheral-to-foveal remapping? A recent study by Chiu & Golomb (2025) provided supporting evidence for peripheral-to-fovea remapping (but not peripheral-to-peripheral remapping) of object-location binding (though in the post-saccadic time window), and suggested foveal prediction as the underlying mechanism.

We thank the reviewer for raising these intriguing questions. We now address them in the revised discussion. We argue that the findings by Harrison et al., 2013 and Szinte et al., 2015 of presaccadic integration of features across two peripheral locations can be explained by presaccadic updating of spatial attention pointers rather than remapping of feature information (pg 8 ln 248-253). The lack of evidence for periphery-to-periphery remapping (Lescroart et al, 2016) and the recent study by Chiu & Golomb (2025) showing object-location binding from periphery to fovea nicely align with our characterization of foveal processing as unique in predicting feature information of upcoming stimuli (pg 8-9 ln 265-269). Finally, we argue that the global (i.e., space-invariant) selection task-irrelevant saccadic target features (Burrows et al., 2014) is well-established at the neural level, but does not suffice to explain the spatially specific nature of foveal prediction (pg 8 ln 220-224). We now include these studies in the revised discussion section.

Reviewer #3 (Public review):

Summary:

In this paper, the authors used fMRI to determine whether peripherally viewed objects could be decoded from the foveal cortex, even when the objects themselves were never viewed foveally. Specifically, they investigated whether pre-saccadic target attributes (shape, semantic category) could be decoded from the foveal cortex. They found that object shape, but not semantic category, could be decoded, providing evidence that foveal feedback relies on low-mid-level information. The authors claim that this provides evidence for a mechanism underlying visual stability and object recognition across saccades.

Strengths:

I think this is another nice demonstration that peripheral information can be decoded from / is processed in the foveal cortex - the methods seem appropriate, and the experiments and analyses are carefully conducted, and the main results seem convincing. The paper itself was very clear and well-written.

We thank the reviewer for this positive evaluation of our work. As discussed in our response to Reviewer 1, we now elaborate on the differences between previous work showing decoding of peripheral information from foveal cortex from the effect shown here. While there are important similarities between these findings, foveal prediction in our study occurs in a saccade condition and in the absence of a task that is specific to stimulus features. 

Weaknesses:

There are a couple of reasons why I think the main theoretical conclusions drawn from the study might not be supported, and why a more thorough investigation might be needed to draw these conclusions.

(1) The authors used a blocked design, with each object being shown repeatedly in the same block. This meant that the stimulus was entirely predictable on each block, which weakens the authors' claims about this being a predictive mechanism that facilitates object recognition - if the stimulus is 100% predictable, there is no aspect of recognition or discrimination actually being tested. I think to strengthen these claims, an experiment would need to have unpredictable stimuli, and potentially combine behavioural reports with decoding to see whether this mechanism can be linked to facilitating object recognition across saccades.

We appreciate the reviewer’s point and would like to highlight that it was not our intention to claim a behavioral effect on object recognition. We believe that an ambiguous formulation in the original abstract may have been interpreted this way, and we thus removed this reference. We also speculated in our Discussion that a potential reason for foveal prediction could be a headstart in peripheral object recognition and in the revised manuscript more clearly highlight that this is a  potential future direction only.

(2)  Given that foveal feedback has been found in previous studies that don't incorporate saccades, how is this a mechanism that might specifically contribute to stability across saccades, rather than just being a general mechanism that aids the processing/discrimination of peripherally-viewed stimuli? I don't think this paper addresses this point, which would seem to be crucial to differentiate the results from those of previous studies.

We fully agree that this point had not been sufficiently addressed in the previous version of the manuscript. As described in our responses to similar comments from reviewers 1 and 2, we included an additional section in the Discussion (“Foveal feedback during saccade preparation”) to more clearly delineate the present study from previous findings of foveal feedback. Previous studies (Williams et al., 2008) only found foveal feedback during narrow discrimination tasks related to spatial features of the target stimulus, not during color-discrimination or fixation-only tasks, concluding that the observed effect must be related to the discrimination behavior. In contrast, we found foveal feedback (as evidenced by decoding of target features) during a saccade condition that was independent of the target features, suggesting a different role of foveal feedback than hypothesized by Williams et al. (2008).

Recommendations for the authors:  

Reviewer #2 (Recommendations for the authors):

(A) Minor comments:

(1)  The task should be clarified earlier in the manuscript.

We now characterise the task in the abstract and clarified its description in the third paragraph, right after introducing the main literature.

(2) Is there actually only 0.5 seconds between saccades? This feels very short/rushed.

The inter-trial-interval was 0.5 seconds, though effectively it varied because the target only appeared once participants fixated on the fixation dot. Note that this pacing is slower than the rate of saccades in natural vision (about 3 to 4 saccades per second).Participants did not report this paradigm as rushed.

(3) Typo on pg2 ln64 (whooe).

Fixed.

(4)  Can the authors also show individual data points for Figures 3 and 4?

We added individual data points for Figures 4 and S2

(5) The MNI coordinates on Figure 4A seem to be incorrect.

We took out those coordinates.

(6) Pg4 ln126 and pg6 ln194, why cite Williams et al. (2008)?

We included this reference here to acknowledge that Williams et al. raised the same issues. We added a “cf.” before this reference to clarify this.

(7) Pg7 ln207 Fabius et al. (2020) showed slow post-saccadic feature remapping, rather than predictive remapping of spatial attention.

We have corrected this mistake.

(8) The OSF link is valid, but I couldn't find a pre-registration.

The issue with the OSF link has been resolved. The pre-registration had been set up but not published. We now published it without changing the original pre-registration (see the screenshot attached).

(9) I couldn't access the OpenNeuro repository.

The issue with the OpenNeuro link has been resolved.

(B) Additional references you may wish to include:

(1) Burrows, B. E., Zirnsak, M., Akhlaghpour, H., Wang, M., & Moore, T.  (2014). Global selection of saccadic target features by neurons in area v4. Journal of Neuroscience.

(2) Chambers, C. D., Allen, C. P., Maizey, L., & Williams, M. A. (2013). Is delayed foveal feedback critical for extra-foveal perception?. Cortex.

(3) Chiu, T. Y., & Golomb, J. D. (2025). The influence of saccade target status on the reference frame of object-location binding. Journal of Experimental Psychology. General.

(4) Harrison, W. J., Retell, J. D., Remington, R. W., & Mattingley, J. B. (2013). Visual crowding at a distance during predictive remapping. Current Biology.

(5) Lescroart, M. D., Kanwisher, N., & Golomb, J. D. (2016). No evidence for automatic remapping of stimulus features or location found with fMRI. Frontiers in Systems Neuroscience.

(6) Moran, C., Johnson, P. A., Hogendoorn, H., & Landau, A. N. (2025). The representation of stimulus features during stable fixation and active vision. Journal of Neuroscience.

(7) Szinte, M., Jonikaitis, D., Rolfs, M., Cavanagh, P., & Deubel, H. (2016). Presaccadic motion integration between current and future retinotopic locations of attended objects. Journal of Neurophysiology.

We thank the reviewer for pointing out these references. We have included them in the revised version of the manuscript.

Reviewer #3 (Recommendations for the authors):

I just have a few minor points where I think some clarifications could be made.

(1) Line 64 - "whooe" should be "whoose" I think.

Fixed.

(2) Around line 53 - you might consider citing this review on foveal feedback - https://doi.org/10.1167/jov.20.12.2

We included the reference (pg 2 ln 55).

(3) Line 129 - you mention a u-shaped relationship for decoding - I wasn't quite sure of the significance/relevance of this relationship - it would be helpful to expand on this / clarify what this means.

We have expanded this section and added statistical tests of the u-shaped relationship in decoding using a weighted quadratic regression. We found significant positive curvature in all early visual areas between fovea and periphery (V1: t(27) = 3.98, p = 0.008, V2: t(27) = 3.03, p = 0.02, V3: t(27)= 2.776, p = 0.025). These findings support a u-shaped relationship. We now report these results in the revised manuscript (pg 5 ln 137-138).

(4) Figure 1 - it would be helpful to indicate how long the target was viewed in the "stim on" panels - I assume it was for the saccade latency, but it would be good to include those values in the main text.

We included that detail in the text (pg 3 ln 96-97).

Author response:

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

Reviewer #1

(1) Related to comment 3, related to the spatial communication section, either provide a clearer worked example or adjust the framing to avoid implying a more developed capability than is shown.

We appreciate the reviewer’s feedback regarding the framing of the spatial communication section. We have removed this section from the revised version.

(2) Related to comment 4 about resolution, consider including explicit numerical estimates of spatial resolution (e.g., median patch diameter in micrometers) for at least one dataset to help users understand practical mapping granularity.

We appreciate the suggestion. We have added explicit numerical estimates of spatial resolution to clarify our mappings. Specifically, we now (i) define “patch” precisely and (ii) report the median patch diameter (in µm) for representative datasets:

10x Visium (mouse cortex): spot diameter = 55 µm; center-to-center spacing = 100 µm.

Slide-seqV2 (mouse brain): bead diameter ≈ 10 µm. When we optionally coarse-grain to 5×5 bead tiles for robustness, the effective patch diameter is ~50 µm

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study examines whether changes in pupil size index prediction-error-related updating during associative learning, formalised as information gain via Kullback-Leibler (KL) divergence. Across two independent tasks, pupil responses scaled with KL divergence shortly after feedback, with the timing and direction of the response varying by task. Overall, the work supports the view that pupil size reflects information-theoretic processes in a context-dependent manner.

Strengths:

This study provides a novel and convincing contribution by linking pupil dilation to informationtheoretic measures, such as KL divergence, supporting Zénon's hypothesis that pupil responses reflect information gain during learning. The robust methodology, including two independent datasets with distinct task structures, enhances the reliability and generalisability of the findings. By carefully analysing early and late time windows, the authors capture the timing and direction of prediction-error-related responses, oPering new insights into the temporal dynamics of model updating. The use of an ideal-learner framework to quantify prediction errors, surprise, and uncertainty provides a principled account of the computational processes underlying pupil responses. The work also highlights the critical role of task context in shaping the direction and magnitude of these ePects, revealing the adaptability of predictive processing mechanisms. Importantly, the conclusions are supported by rigorous control analyses and preprocessing sanity checks, as well as convergent results from frequentist and Bayesian linear mixed-ePects modelling approaches.

Weaknesses:

Some aspects of directionality remain context-dependent, and on current evidence cannot be attributed specifically to whether average uncertainty increases or decreases across trials. DiPerences between the two tasks (e.g., sensory modality and learning regime) limit direct comparisons of ePect direction and make mechanistic attribution cautious. In addition, subjective factors such as confidence were not measured and could influence both predictionerror signals and pupil responses. Importantly, the authors explicitly acknowledge these limitations, and the manuscript clearly frames them as areas for future work rather than settled conclusions.

Reviewer #2 (Public review):

Summary:

The authors investigate whether pupil dilation reflects information gain during associative learning, formalised as Kullback-Leibler divergence within an ideal observer framework. They examine pupil responses in a late time window after feedback and compare these to informationtheoretic estimates (information gain, surprise, and entropy) derived from two diPerent tasks with contrasting uncertainty dynamics.

Strength:

The exploration of task evoked pupil dynamics beyond the immediate response/feedback period and then associating them with model estimates was interesting and inspiring. This oPered a new perspective on the relationship between pupil dilation and information processing.

Weakness:

However, the interpretability of the findings remains constrained by the fundamental diPerences between the two tasks (stimulus modality, feedback type, and learning structure), which confound the claimed context-dependent ePects. The later time-window pupil ePects, although intriguing, are small in magnitude and may reflect residual noise or task-specific arousal fluctuations rather than distinct information-processing signals. Thus, while the study oPers valuable methodological insight and contributes to ongoing debates about the role of the pupil in cognitive inference, its conclusions about the functional significance of late pupil responses should be treated with caution.

Reviewer #3 (Public review):

Summary:

Thank you for inviting me to review this manuscript entitled "Pupil dilation oPers a time-window on prediction error" by Colizoli and colleagues. The study examines prediction errors, information gain (Kullback-Leibler [KL] divergence), and uncertainty (entropy) from an information-theory perspective using two experimental tasks and pupillometry. The authors aim to test a theoretical proposal by Zénon (2019) that the pupil response reflects information gain (KL divergence). The conclusion of this work is that (post-feedback) pupil dilation in response to information gain is context dependent.

Strengths:

Use of an established Bayesian model to compute KL divergence and entropy.

Pupillometry data preprocessing and multiple robustness checks.

Weaknesses:

Operationalization of prediction errors based on frequency, accuracy, and their interaction:

The authors rely on a more model-agnostic definition of the prediction error in terms of stimulus frequency ("unsigned prediction error"), accuracy, and their interaction ("signed prediction error"). While I see the point, I would argue that this approach provides a simple approximation of the prediction error, but that a model-based approach would be more appropriate.

Model validation:

My impression is that the ideal learner model should work well in this case. However, the authors don't directly compare model behavior to participant behavior ("posterior predictive checks") to validate the model. Therefore, it is currently unclear if the model-derived terms like KL divergence and entropy provide reasonable estimates for the participant data.

Lack of a clear conclusion:

The authors conclude that this study shows for the first time that (post-feedback) pupil dilation in response to information gain is context dependent. However, the study does not oPer a unifying explanation for such context dependence. The discussion is quite detailed with respect to taskspecific ePects, but fails to provide an overarching perspective on the context-dependent nature of pupil signatures of information gain. This seems to be partly due to the strong diPerences between the experimental tasks.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I highly appreciate the care and detail in the authors' response and thank them for the ePort invested in revising the manuscript. They addressed the core concerns to a high standard, and the manuscript has substantially improved in methodological rigour (through additional controls/sanity checks and complementary mixed-ePects analyses) and in clarity of interpretation (by explicitly acknowledging context-dependence and tempering stronger claims). The present version reads clearly and is much strengthened overall. I only have a few minor points below:

Minor suggestions:

Abstract:

In the abstract KL is introduced as abbreviation, but at first occurence it should be written out as "Kullback-Leibler (KL)" for readers not familiar with it.

We thank the reviewer for catching this error. It has been correct in the version of record.

Methods:

I appreciate the additional bayesian LME analysis. I only had a few things that I thought were missing from knowing the parameters: 1) what was the target acceptance rate (default of .95?), 2) which family was used to model the response distribution: (default) "gaussian" or robust "student-t"? Depending on the data a student-t would be preferred, but since the author's checked the fit & the results corroborate the correlation analysis, using the default would also be fine! Just add the information for completeness.

Thank you for bringing this to our attention. We have now noted that default parameters were used in all cases unless otherwise mentioned. 

Thank you once again for your time and consideration.

Reviewer #2 (Recommendations for the authors):

Thanks to the authors' ePort on revision. I am happy with this new version of manuscript.

Thank you once again for your time and consideration.

Reviewer #3 (Recommendations for the authors):

(1) Regarding comments #3 and #6 (first round) on model validation and posterior predictive checks, the authors replied that since their model is not a "generative" one, they can't perform posterior predictive checks. Crucially, in eq. 2, the authors present the p{tilde}^j_k variable denoting the learned probability of event k on trial j. I don't see why this can't be exploited for simulations. In my opinion, one could (and should) generate predictions based on this variable. The simplest implementation would translate the probability into a categorical choice (w/o fitting any free parameter). Based on this, they could assess whether the model and data are comparable.

We thank the reviewer for this clarification. The reviewer suggests using the probability distributions at each trial to predict which event should be chosen on each trial. More specifically, the event(s) with the highest probability on trial j could be used to generate a prediction for the choice of the participant on trial j. We agree that this would indeed be an interesting analysis. However, the response options of each task are limited to two-alternatives. In the cue-target task, four events are modeled (representing all possible cue-target conditions) while the participants’ response options are only “left” and “right”. Similarly, in the letter-color task, 36 events are modeled while the participants’ response options are “match” and “no-match”. In other words, we do not know which event (either four or 36, for the two tasks) the participant would have indicated on each trial. As an approximation to this fine-grained analysis, we investigated the relationship between the information-theoretic variables separately for error and correct trials. Our rationale was that we would have more insight into how the model fits depended on the participants’ actual behavior as compared with the ideal learner model.

(2) I recommend providing a plot of the linear mixed model analysis of the pupil data. Currently, results are only presented in the text and tables, but a figure would be much more useful.

We thank the reviewer for the suggestion to add a plot of the linear mixed model results. We appreciate the value of visualizing model estimates; however, we feel that the current presentation in the text and tables clearly conveys the relevant findings. For this reason, and to avoid further lengthening the manuscript, we prefer to retain the current format.

(3) I would consider only presenting the linear mixed ePects for the pupil data in the main results, and the correlation results in the supplement. It is currently quite long.

We thank the reviewer for this recommendation. We agree that the results section is detailed; however, we consider the correlation analyses to be integral to the interpretation of the pupil data and therefore prefer to keep them in the main text rather than move them to the supplement.

The following is the authors’ response to the original reviews

eLife Assessment

This important study seeks to examine the relationship between pupil size and information gain, showing opposite effects dependent upon whether the average uncertainty increases or decreases across trials. Given the broad implications for learning and perception, the findings will be of broad interest to researchers in cognitive neuroscience, decision-making, and computational modelling. Nevertheless, the evidence in support of the particular conclusion is at present incomplete - the conclusions would be strengthened if the authors could both clarify the differences between model-updating and prediction error in their account and clarify the patterns in the data.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study investigates whether pupil dilation reflects prediction error signals during associative learning, defined formally by Kullback-Leibler (KL) divergence, an information-theoretic measure of information gain. Two independent tasks with different entropy dynamics (decreasing and increasing uncertainty) were analyzed: the cue-target 2AFC task and the lettercolor 2AFC task. Results revealed that pupil responses scaled with KL divergence shortly after feedback onset, but the direction of this relationship depended on whether uncertainty (entropy) increased or decreased across trials. Furthermore, signed prediction errors (interaction between frequency and accuracy) emerged at different time windows across tasks, suggesting taskspecific temporal components of model updating. Overall, the findings highlight that pupil dilation reflects information-theoretic processes in a complex, context-dependent manner.

Strengths:

This study provides a novel and convincing contribution by linking pupil dilation to informationtheoretic measures, such as KL divergence, supporting Zénon's hypothesis that pupil responses reflect information gained during learning. The robust methodology, including two independent datasets with distinct entropy dynamics, enhances the reliability and generalisability of the findings. By carefully analysing early and late time windows, the authors capture the temporal dynamics of prediction error signals, offering new insights into the timing of model updates. The use of an ideal learner model to quantify prediction errors, surprise, and entropy provides a principled framework for understanding the computational processes underlying pupil responses. Furthermore, the study highlights the critical role of task context - specifically increasing versus decreasing entropy - in shaping the directionality and magnitude of these effects, revealing the adaptability of predictive processing mechanisms.

Weaknesses:

While this study offers important insights, several limitations remain. The two tasks differ significantly in design (e.g., sensory modality and learning type), complicating direct comparisons and limiting the interpretation of differences in pupil dynamics. Importantly, the apparent context-dependent reversal between pupil constriction and dilation in response to feedback raises concerns about how these opposing effects might confound the observed correlations with KL divergence. 

We agree with the reviewer’s concerns and acknowledge that the speculation concerning the directional effect of entropy across trials can not be fully substantiated by the current study. As the reviewer points out, the directional relationship between pupil dilation and information gain must be due to other factors, for instance, the sensory modality, learning type, or the reversal between pupil constriction and dilation across the two tasks. Also, we would like to note that ongoing experiments in our lab already contradict our original speculation. In line with the reviewer’s point, we noted these differences in the section on “Limitations and future research” in the Discussion. To better align the manuscript with the above mentioned points, we have made several changes in the Abstract, Introduction and Discussion summarized below: 

We have removed the following text from the Abstract and Introduction: “…, specifically related to increasing or decreasing average uncertainty (entropy) across trials.”

We have edited the following text in the Introduction (changes in italics) (p. 5):

“We analyzed two independent datasets featuring distinct associative learning paradigms, one characterized by increasing entropy and the other by decreasing entropy as the tasks progressed. By examining these different tasks, we aimed to identify commonalities (if any) in the results across varying contexts. Additionally, the contrasting directions of entropy in the two tasks enabled us to disentangle the correlation between stimulus-pair frequency and information gain in the postfeedback pupil response.

We have removed the following text from the Discussion:

“…and information gain in fact seems to be driven by increased uncertainty.”

“We speculate that this difference in the direction of scaling between information gain and the pupil response may depend on whether entropy was increasing or decreasing across trials.” 

“…which could explain the opposite direction of the relationship between pupil dilation and information gain”

“… and seems to relate to the direction of the entropy as learning progresses (i.e., either increasing or decreasing average uncertainty).” 

We have edited the following texts in the Discussion (changes in italics):

“For the first time, we show that the direction of the relationship between postfeedback pupil dilation and information gain (defined as KL divergence) was context dependent.” (p. 29):

Finally, we have added the following correction to the Discussion (p. 30):

“Although it is tempting to speculate that the direction of the relationship between pupil dilation and information gain may be due to either increasing or decreasing entropy as the task progressed, we must refrain from this conclusion. We note that the two tasks differ substantially in terms of design with other confounding variables and therefore cannot be directly compared to one another. We expand on these limitations in the section below (see Limitations and future research).”

Finally, subjective factors such as participants' confidence and internal belief states were not measured, despite their potential influence on prediction errors and pupil responses.

Thank you for the thoughtful comment. We agree with the reviewer that subjective factors, such as participants' confidence, can be important in understanding prediction errors and pupil responses. As per the reviewer’s point, we have included the following limitation in the Discussion (p. 33): 

“Finally, while we acknowledge the potential relevance of subjective factors, such as the participants’ overt confidence reports, in understanding prediction errors and pupil responses, the current study focused on the more objective, model-driven measure of information-theoretic variables. This approach aligns with our use of the ideal learner model, which estimates information-theoretic variables while being agnostic about the observer's subjective experience itself. Future research is needed to explore the relationship between information-gain signals in pupil dilation and the observer’s reported experience of or awareness about confidence in their decisions.” 

Reviewer #2 (Public review):

Summary:

The authors proposed that variability in post-feedback pupillary responses during the associative learning tasks can be explained by information gain, which is measured as KL divergence. They analysed pupil responses in a later time window (2.5s-3s after feedback onset) and correlated them with information-theory-based estimates from an ideal learner model (i.e., information gain-KL divergence, surprise-subjective probability, and entropy-average uncertainty) in two different associative decision-making tasks.

Strength:

The exploration of task-evoked pupil dynamics beyond the immediate response/feedback period and then associating them with model estimates was interesting and inspiring. This offered a new perspective on the relationship between pupil dilation and information processing.

Weakness:

However, disentangling these later effects from noise needs caution. Noise in pupillometry can arise from variations in stimuli and task engagement, as well as artefacts from earlier pupil dynamics. The increasing variance in the time series of pupillary responses (e.g., as shown in Figure 2D) highlights this concern.

It's also unclear what this complicated association between information gain and pupil dynamics actually means. The complexity of the two different tasks reported made the interpretation more difficult in the present manuscript.

We share the reviewer’s concerns. To make this point come across more clearly, we have added the following text to the Introduction (p. 5):

“The current study was motivated by Zenon’s hypothesis concerning the relationship between pupil dilation and information gain, particularly in light of the varying sources of signal and noise introduced by task context and pupil dynamics. By demonstrating how task context can influence which signals are reflected in pupil dilation, and highlighting the importance of considering their temporal dynamics, we aim to promote a more nuanced and model-driven approach to cognitive research using pupillometry.”

Reviewer #3 (Public review):

Summary:

This study examines prediction errors, information gain (Kullback-Leibler [KL] divergence), and uncertainty (entropy) from an information-theory perspective using two experimental tasks and pupillometry. The authors aim to test a theoretical proposal by Zénon (2019) that the pupil response reflects information gain (KL divergence). In particular, the study defines the prediction error in terms of KL divergence and speculates that changes in pupil size associated with KL divergence depend on entropy. Moreover, the authors examine the temporal characteristics of pupil correlates of prediction errors, which differed considerably across previous studies that employed different experimental paradigms. In my opinion, the study does not achieve these aims due to several methodological and theoretical issues.

Strengths:

(1)  Use of an established Bayesian model to compute KL divergence and entropy.

(2)  Pupillometry data preprocessing, including deconvolution.

Weaknesses:

(1) Definition of the prediction error in terms of KL divergence:

I'm concerned about the authors' theoretical assumption that the prediction error is defined in terms of KL divergence. The authors primarily refer to a review article by Zénon (2019): "Eye pupil signals information gain". It is my understanding that Zénon argues that KL divergence quantifies the update of a belief, not the prediction error: "In short, updates of the brain's internal model, quantified formally as the Kullback-Leibler (KL) divergence between prior and posterior beliefs, would be the common denominator to all these instances of pupillary dilation to cognition." (Zénon, 2019).

From my perspective, the update differs from the prediction error. Prediction error refers to the difference between outcome and expectation, while update refers to the difference between the prior and the posterior. The prediction error can drive the update, but the update is typically smaller, for example, because the prediction error is weighted by the learning rate to compute the update. My interpretation of Zénon (2019) is that they explicitly argue that KL divergence defines the update in terms of the described difference between prior and posterior, not the prediction error.

The authors also cite a few other papers, including Friston (2010), where I also could not find a definition of the prediction error in terms of KL divergence. For example [KL divergence:] "A non-commutative measure of the non-negative difference between two probability distributions." Similarly, Friston (2010) states: Bayesian Surprise - "A measure of salience based on the Kullback-Leibler divergence between the recognition density (which encodes posterior beliefs) and the prior density. It measures the information that can be recognized in the data." Finally, also in O'Reilly (2013), KL divergence is used to define the update of the internal model, not the prediction error.

The authors seem to mix up this common definition of the model update in terms of KL divergence and their definition of prediction error along the same lines. For example, on page 4: "KL divergence is a measure of the difference between two probability distributions. In the context of predictive processing, KL divergence can be used to quantify the mismatch between the probability distributions corresponding to the brain's expectations about incoming sensory input and the actual sensory input received, in other words, the prediction error (Friston, 2010; Spratling, 2017)."

Similarly (page 23): "In the current study, we investigated whether the pupil's response to decision outcome (i.e., feedback) in the context of associative learning reflects a prediction error as defined by KL divergence."

This is problematic because the results might actually have limited implications for the authors' main perspective (i.e., that the pupil encodes prediction errors) and could be better interpreted in terms of model updating. In my opinion, there are two potential ways to deal with this issue:

(a) Cite work that unambiguously supports the perspective that it is reasonable to define the prediction error in terms of KL divergence and that this has a link to pupillometry. In this case, it would be necessary to clearly explain the definition of the prediction error in terms of KL divergence and dissociate it from the definition in terms of model updating.

(b) If there is no prior work supporting the authors' current perspective on the prediction error, it might be necessary to revise the entire paper substantially and focus on the definition in terms of model updating.

We thank the reviewer for pointy out these inconsistencies in the manuscript and appreciate their suggestions for improvement. We take approach (a) recommended by the reviewer, and provide our reasoning as to why prediction error signals in pupil dilation are expected to correlate with information gain (defined as the KL divergence between posterior and prior belief distributions). This can be found in a new section in the introduction, copied here for convenience (p. 3-4):

“We reasoned that the link between prediction error signals and information gain in pupil dilation is through precision-weighting. Precision refers to the amount of uncertainty (inverse variance) of both the prior belief and sensory input in the prediction error signals [6,64–67]. More precise prediction errors receive more weighting, and therefore, have greater influence on model updating processes. The precisionweighting of prediction error signals may provide a mechanism for distinguishing between known and unknown sources of uncertainty, related to the inherent stochastic nature of a signal versus insufficient information of the part of the observer, respectively [65,67,68]. In Bayesian frameworks, information gain is fundamentally linked to prediction error, modulated by precision [65,66,69–75]. In non-hierarchical Bayesian models, information gain can be derived as a function of prediction errors and the precision of the prior and likelihood distributions, a relationship that can be approximately linear [70]. In hierarchical Bayesian inference, the update in beliefs (posterior mean changes) at each level is proportional to the precision-weighted prediction error; this update encodes the information gained from new observations [65,66,69,71,72]. Neuromodulatory arousal systems are well-situated to act as precision-weighting mechanisms in line with predictive processing frameworks [76,77]. Empirical evidence suggests that neuromodulatory systems broadcast precisionweighted prediction errors to cortical regions [11,59,66,78]. Therefore, the hypothesis that feedback-locked pupil dilation reflects a prediction error signal is similarly in line with Zenon’s main claim that pupil dilation generally reflects information gain, through precision-weighting of the prediction error. We expected a prediction error signal in pupil dilation to be proportional to the information gain.”

We have referenced previous work that has linked prediction error and information gain directly (p. 4): “The KL divergence between posterior and prior belief distributions has been previously considered to be a proxy of (precision-weighted) prediction errors [68,72].”

We have taken the following steps to remedy this error of equating “prediction error” directly with the information gain.

First, we have replaced “KL divergence” with “information gain” whenever possible throughout the manuscript for greater clarity. 

Second, we have edited the section in the introduction defining information gain substantially (p. 4): 

“Information gain can be operationalized within information theory as the KullbackLeibler (KL) divergence between the posterior and prior belief distributions of a Bayesian observer, representing a formalized quantity that is used to update internal models [29,79,80]. Itti and Baldi (2005)81 termed the KL divergence between posterior and prior belief distributions as “Bayesian surprise” and showed a link to the allocation of attention. The KL divergence between posterior and prior belief distributions has been previously considered to be a proxy of (precision-weighted) prediction errors[68,72]. According to Zénon’s hypothesis, if pupil dilation reflects information gain during the observation of an outcome event, such as feedback on decision accuracy, then pupil size will be expected to increase in proportion to how much novel sensory evidence is used to update current beliefs [29,63]. ” 

Finally, we have made several minor textual edits to the Abstract and main text wherever possible to further clarify the proposed relationship between prediction errors and information gain.

(2) Operationalization of prediction errors based on frequency, accuracy, and their interaction:

The authors also rely on a more model-agnostic definition of the prediction error in terms of stimulus frequency ("unsigned prediction error"), accuracy, and their interaction ("signed prediction error"). While I see the point here, I would argue that this approach offers a simple approximation to the prediction error, but it is possible that factors like difficulty and effort can influence the pupil signal at the same time, which the current approach does not take into account. I recommend computing prediction errors (defined in terms of the difference between outcome and expectation) based on a simple reinforcement-learning model and analyzing the data using a pupillometry regression model in which nuisance regressors are controlled, and results are corrected for multiple comparisons.

We agree with the reviewer’s suggestion that alternatively modeling the data in a reinforcement learning paradigm would be fruitful. We adopted the ideal learner model as we were primarily focused on Information Theory, stemming from our aim to test Zenon’s hypothesis that information gain drives pupil dilation. However, we agree with the reviewer that it is worthwhile to pursue different modeling approaches in future work. We have now included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times (explained in more detail below in our response to your point #4). Results including correction for multiple comparisons was reported for all pupil time course data as detailed in Methods section 2.5. 

(3) The link between model-based (KL divergence) and model-agnostic (frequency- and accuracy-based) prediction errors:

I was expecting a validation analysis showing that KL divergence and model-agnostic prediction errors are correlated (in the behavioral data). This would be useful to validate the theoretical assumptions empirically.

The model limitations and the operalization of prediction error in terms of post-feedback processing do not seem to allow for a comparison of information gain and model-agnostic prediction errors in the behavioral data for the following reasons. First, the simple ideal learner model used here is not a generative model, and therefore, cannot replicate or simulate the participants responses (see also our response to your point #6 “model validation” below). Second, the behavioral dependent variables obtained are accuracy and reaction times, which both occur before feedback presentation. While accuracy and reaction times can serve as a marker of the participant’s (statistical) confidence/uncertainty following the decision interval, these behavioral measures cannot provide access to post-feedback information processing. The pupil dilation is of interest to us because the peripheral arousal system is able to provide a marker of post-feedback processing. Through the analysis presented in Figure 3, we indeed aimed to make the comparison of the model-based information gain to the model-agnostic prediction errors via the proxy variable of post-feedback pupil dilation instead of behavioral variables. To bridge the gap between the “behaviorally agnostic” model parameters and the actual performance of the participants, we examined the relationship between the model-based information gain and the post-feedback pupil dilation separately for error and correct trials as shown in Figure 3D-F & Figure 3J-L. We hope this addresses the reviewers concern and apologize in case we did not understand the reviewers suggestion here.

(4) Model-based analyses of pupil data:

I'm concerned about the authors' model-based analyses of the pupil data. The current approach is to simply compute a correlation for each model term separately (i.e., KL divergence, surprise, entropy). While the authors do show low correlations between these terms, single correlational analyses do not allow them to control for additional variables like outcome valence, prediction error (defined in terms of the difference between outcome and expectation), and additional nuisance variables like reaction time, as well as x and y coordinates of gaze.

Moreover, including entropy and KL divergence in the same regression model could, at least within each task, provide some insights into whether the pupil response to KL divergence depends on entropy. This could be achieved by including an interaction term between KL divergence and entropy in the model.

In line with the reviewer’s suggestions, we have included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times. We compared the performance of two models on the post-feedback pupil dilation in each time window of interest: Modle 1 had no interaction between information gain and entropy and Model 2 included an interaction term as suggested. We did not include the x- and y- coordinates of gaze in the mixed linear model analysis, as there are multiple values of these coordinates per trial. Furthermore, regressing out the x and y- coordinates of gaze can potentially remove signal of interest in the pupil dilation data in addition to the gaze-related confounds and we did not measure absolute pupil size (Mathôt, Melmi & Castet, 2015; Hayes & Petrov, 2015). We present more sanity checks on the pre-processing pipeline as recommended by Reviewer 1.  

This new analysis resulted in several additions to the Methods (see Section 2.5) and Results. In sum, we found that including an interaction term for information gain and entropy did not lead to better model fits, but sometimes lead to significantly worse fits. Overall, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the pre-feedback baseline pupil and preceeding reaction time differences. There was only one difference to note between the correlation and linear mixed modeling analyses: for the error trials in the cue-target 2AFC task, including entropy in the model accounted for the variance previously explained by surprise.

(5) Major differences between experimental tasks:

More generally, I'm not convinced that the authors' conclusion that the pupil response to KL divergence depends on entropy is sufficiently supported by the current design. The two tasks differ on different levels (stimuli, contingencies, when learning takes place), not just in terms of entropy. In my opinion, it would be necessary to rely on a common task with two conditions that differ primarily in terms of entropy while controlling for other potentially confounding factors. I'm afraid that seemingly minor task details can dramatically change pupil responses. The positive/negative difference in the correlation with KL divergence that the authors interpret to be driven by entropy may depend on another potentially confounding factor currently not controlled.

We agree with the reviewer’s concerns and acknowledge that the speculation concerning the directional effect of entropy across trials can not be fully substantiated by the currect study. We note that Review #1 had a similar concern. Our response to Reviewer #1 addresses this concern of Reviewer #3 as well. To better align the manuscript with the above mentioned points, we have made several changes that are detailed in our response to Reviewer #1’s public review (above). 

(6) Model validation:

My impression is that the ideal learner model should work well in this case. However, the authors don't directly compare model behavior to participant behavior ("posterior predictive checks") to validate the model. Therefore, it is currently unclear if the model-derived terms like KL divergence and entropy provide reasonable estimates for the participant data.

Based on our understanding, posterior predictive checks are used to assess the goodness of fit between generated (or simulated) data and observed data. Given that the “simple” ideal learner model employed in the current study is not a generative model, a posterior predictive check would not apply here (Gelman, Carlin, Stern, Dunson, Vehtari, & Rubin (2013). The ideal learner model is unable to simulate or replicate the participants’ responses and behaviors such as accuracy and reaction times; it simply computes the probability of seeing each stimulus type at each trial based on the prior distribution and the exact trial order of the stimuli presented to each participant. The model’s probabilities are computed directly from a Dirichlet distribution of values that represent the number of occurences of each stimulus-pair type for each task. The information-theoretic variables are then directly computed from these probabilities using standard formulas. The exact formulas used in the ideal learner model can be found in section 2.4.

We have now included a complementary linear mixed model analysis which also provides insight into the amount of explained variance of these information-theoretic predictors on the post-feedback pupil response, while also including the pre-feedback baseline pupil and reaction time differences (see section 3.3, Tables 3 & 4). The R² values ranged from 0.16 – 0.50 across all conditions tested.

(7) Discussion:

The authors interpret the directional effect of the pupil response w.r.t. KL divergence in terms of differences in entropy. However, I did not find a normative/computational explanation supporting this interpretation. Why should the pupil (or the central arousal system) respond differently to KL divergence depending on differences in entropy?

The current suggestion (page 24) that might go in this direction is that pupil responses are driven by uncertainty (entropy) rather than learning (quoting O'Reilly et al. (2013)). However, this might be inconsistent with the authors' overarching perspective based on Zénon (2019) stating that pupil responses reflect updating, which seems to imply learning, in my opinion. To go beyond the suggestion that the relationship between KL divergence and pupil size "needs more context" than previously assumed, I would recommend a deeper discussion of the computational underpinnings of the result.

Since we have removed the original speculative conclusion from the manuscript, we will refrain from discussing the computational underpinnings of a potential mechanism. To note as mentioned above, we have preliminary data from our own lab that contradicts our original hypothesis about the relationship between entropy and information gain on the post-feedback pupil response. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Apart from the points raised in the public review above, I'd like to use the opportunity here to provide a more detailed review of potential issues, questions, and queries I have:

(1) Constriction vs. Dilation Effects:

The study observes a context-dependent relationship between KL divergence and pupil responses, where pupil dilation and constriction appear to exhibit opposing effects. However, this phenomenon raises a critical concern: Could the initial pupil constriction to visual stimuli (e.g., in the cue-target task) confound correlations with KL divergence? This potential confound warrants further clarification or control analyses to ensure that the observed effects genuinely reflect prediction error signals and are not merely a result of low-level stimulus-driven responses.

We agree with the reviewers concern and have added the following information to the limitations section in the Discussion (changes in italics below; p. 32-33).

“First, the two associative learning paradigms differed in many ways and were not directly comparable. For instance, the shape of the mean pupil response function differed across the two tasks in accordance with a visual or auditory feedback stimulus (compare Supplementary Figure 3A with Supplementary Figure 3D), and it is unclear whether these overall response differences contributed to any differences obtained between task conditions within each task. We are unable to rule out whether so-called “low level” effects such as the initial constriction to visual stimuli in the cue-target 2AFC task as compared with the dilation in response auditory stimuli in letter-color 2AFC task could confound correlations with information gain. Future work should strive to disentangle how the specific aspects of the associative learning paradigms relate to prediction errors in pupil dilation by systematically manipulating design elements within each task.”

Here, I also was curious about Supplementary Figure 1, showing 'no difference' between the two tones (indicating 'error' or 'correct'). Was this the case for FDR-corrected or uncorrected cluster statistics? Especially since the main results also showed sig. differences only for uncorrected cluster statistics (Figure 2), but were n.s. for FDR corrected. I.e. can we be sure to rule out a confound of the tones here after all?

As per the reviewer’s suggestion, we verified that there were also no significant clusters after feedback onset before applying the correction for multiple comparisons. We have added this information to Supplemenatary section 1.2 as follows: 

“Results showed that the auditory tone dilated pupils on average (Supplementary Figure 1C). Crucially, however, the two tones did not differ from one another in either of the time windows of interest (Supplementary Figure 1D; no significant time points after feedback onset were obtained either before or after correcting for multiple comparisons using cluster-based permutation methods; see Section 2.5.” 

Supplementary Figure 1 is showing effects cluster-corrected for multiple comparisons using cluster-based permutation tests from the MNE software package in Python (see Methods section 2.5). We have clarified that the cluster-correction was based on permutation testing in the figure legend. 

(2) Participant-Specific Priors:

The ideal learner models do not account for individualised priors, assuming homogeneous learning behaviour across participants. Could incorporating participant-specific priors better reflect variability in how individuals update their beliefs during associative learning?

We have clarified in the Methods (see section 2.4) that the ideal learner models did account for participant-specific stimuli including participant-specific priors in the letter-color 2AFC task. We have added the following texts: 

“We also note that while the ideal learner model for the cue-target 2AFC task used a uniform (flat) prior distribution for all participants, the model parameters were based on the participant-specific cue-target counterbalancing conditions and randomized trial order.” (p. 13)

“The prior distributions used for the letter-color 2AFC task were estimated from the randomized letter-color pairs and randomized trial order presentation in the preceding odd-ball task; this resulted in participant-specific prior distributions for the ideal learner model of the letter-color 2AFC task. The model parameters were likewise estimated from the (participant-specific) randomized trial order presented in the letter-color 2AFC task.” (p. 13)

(3) Trial-by-Trial Variability:

The analysis does not account for random effects or inter-trial variability using mixed-effects models. Including such models could provide a more robust statistical framework and ensure the observed relationships are not influenced by unaccounted participant- or trial-specific factors.

We have included a complementary linear mixed model analysis in which “subject” was modeled as a random effect on the post-feedback pupil response in each time window of interest and for each task. Across all trials, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the prefeedback baseline pupil and preceeding reaction time differences (see section 3.3, Tables 3 & 4).

(4) Preprocessing/Analysis choices:

Before anything else, I'd like to highlight the authors' effort in providing public code (and data) in a very readable and detailed format!

We appreciate the compliment - thank you for taking the time to look at the data and code provided.

I found the idea of regressing the effect of Blinks/Saccades on the pupil trace intriguing. However, I miss a complete picture here to understand how well this actually worked, especially since it seems to be performed on already interpolated data. My main points here are:

(4.1) Why is the deconvolution performed on already interpolated data and not on 'raw' data where there are actually peaks of information to fit?

To our understanding, at least one critical reason for interpolating the data before proceeding with the deconvolution analysis is that the raw data contain many missing values (i.e., NaNs) due to the presence of blinks. Interpolating over the missing data first ensures that there are valid numerical elements in the linear algebra equations. We refer the reviewer to the methods detailed in Knapen et al. (2016) for more details on this pre-processing method. 

(4.2) What is the model fit (e.g. R-squared)? If this was a poor fit for the regressors in the first place, can we trust the residuals (i.e. clean pupil trace)? Is it possible to plot the same Pupil trace of Figure 1D with a) the 'raw' pupil time-series, b) after interpolation only (both of course also mean-centered for comparison), on top of the residuals after deconvolution (already presented), so we can be sure that this is not driving the effects in a 'bad' way? I'd just like to make sure that this approach did not lead to artefacts in the residuals rather than removing them.

We thank the reviewer for this suggestion. In the Supplementary Materials, we have included a new figure (Supplementary Figure 2, copied below for convience), which illustrates the same conditions as in Figure 1D and Figure 2D, with 1) the raw data, and 2) the interpolated data before the nuisance regression. Both the raw data and interpolated data have been band-pass filtered as was done in the original pre-processing pipeline and converted to percent signal change. These figures can be compared directly to Figure 1D and Figure 2D, for the two tasks, respectively. 

Of note is that the raw data seem to be dominated by responses to blinks (and/or saccades). Crucially, the pattern of results remains overall unchaged between the interpolated-only and fully pre-processed version of the data for both tasks. 

In the Supplementary Materials (see Supplementary section 2), we have added the descriptives of the model fits from the deconvolution method. Model fits (R²) for the nuisance regression were generally low: cue-target 2AFC task, M = 0.03, SD = 0.02, range = [0.00, 0.07]; letter-color visual 2AFC, M = 0.08, SD = 0.04, range = [0.02, 0.16].

Furthermore, a Pearson correlation analysis between the interpolated and fully pre-processed data within the time windows of interest for both task indicated high correspondence: 

Cue-target 2AFC task

Early time window: M = 0.99, SD = 0.01, range = [0.955, 1.000]

Late time window: M = 0.99, SD = 0.01, range = [0.971, 1.000]

Letter-color visual 2AFC

Early time window: M = 0.95, SD = 0.04, range = [0.803, 0.998]

Late time window: M = 0.97, SD = 0.02, range = [0.908, 0.999]

In hindsight, including the deconvolution (nuisance regression) method may not have changed the pattern of results much. However, the decision to include this deconvolution method was not data-driven; instead, it was based on the literature establishing the importance of removing variance (up to 5 s) of these blinks and saccades from cognitive effects of interest in pupil dilation (Knapen et al., 2016). 

(4.3) Since this should also lead to predicted time series for the nuisance-regressors, can we see a similar effect (of what is reported for the pupil dilation) based on the blink/saccade traces of a) their predicted time series based on the deconvolution, which could indicate a problem with the interpretation of the pupil dilation effects, and b) the 'raw' blink/saccade events from the eye-tracker? I understand that this is a very exhaustive analysis so I would actually just be interested here in an averaged time-course / blink&saccade frequency of the same time-window in Figure 1D to complement the PD analysis as a sanity check.

Also included in the Supplementary Figure 2 is the data averaged as in Figure 1D and Figure 2D for the raw data and nuisance-predictor time courses (please refer to the bottom row of the sub-plots). No pattern was observed in either the raw data or the nuisance predictors as was shown in the residual time courses. 

(4.4) How many samples were removed from the time series due to blinks/saccades in the first place? 150ms for both events in both directions is quite a long bit of time so I wonder how much 'original' information of the pupil was actually left in the time windows of interest that were used for subsequent interpretations.

We thank the reviewer for bringing this issue to our attention. The size of the interpolation window was based on previous literature, indicating a range of 100-200 ms as acceptable (Urai et al., 2017; Knapen et al., 2016; Winn et al., 2018). The ratio of interpolated-to-original data (across the entire trial) varied greatly between participants and between trials: cue-target 2AFC task, M = 0.262, SD = 0.242, range = [0,1]; letter-color 2AFC task, M = 0.194, SD = 0.199, range = [0,1]. 

We have now included a conservative analysis in which only trials with more than half (threshold = 60%) of original data are included in the analyses. Crucially, we still observe the same pattern of effects as when all data are considered across both tasks (compare the second to last row in the Supplementary Figure 2 to Figure 1D and Figure 2D).

(4.5) Was the baseline correction performed on the percentage change unit?

Yes, the baseline correction was performed on the pupil timeseries after converting to percentsignal change. We have added that information to the Methods (section 2.3).

(4.6) What metric was used to define events in the derivative as 'peaks'? I assume some sort of threshold? How was this chosen?

The threshold was chosen in a data-driven manner and was kept consistent across both tasks. The following details have been added to the Methods:

“The size of the interpolation window preceding nuisance events was based on previous literature [13,39,99]. After interpolation based on data-markers and/or missing values, remaining blinks and saccades were estimated by testing the first derivative of the pupil dilation time series against a threshold rate of change. The threshold for identifying peaks in the temporal derivative is data-driven, partially based on past work[10,14,33]. The output of each participant’s pre-processing pipeline was checked visually. Once an appropriate threshold was established at the group level, it remained the same for all participants (minimum peak height of 10 units).” (p. 8 & 11).

(5) Multicollinearity Between Variables:

Lastly, the authors state on page 13: "Furthermore, it is expected that these explanatory variables will be correlated with one another. For this reason, we did not adopt a multiple regression approach to test the relationship between the information-theoretic variables and pupil response in a single model". However, the very purpose of multiple regression is to account for and disentangle the contributions of correlated predictors, no? I might have missed something here.

We apologize for the ambiguity of our explanation in the Methods section. We originally sought to assess the overall relationship between the post-feedback response and information gain (primarily), but also surprise and entropy. Our reasoning was that these variables are often investigated in isolation across different experiments (i.e., only investigating Shannon surprise), and we would like to know what the pattern of results would look like when comparing a single information-theoretic variable to the pupil response (one-by-one). We assumed that including additional explanatory variables (that we expected to show some degree of collinearity with each other) in a regression model would affect variance attributed to them as compared with the one-on-one relationships observed with the pupil response (Morrissey & Ruxton 2018). We also acknowledge the value of a multiple regression approach on our data. Based on the suggestions by the reviewers we have included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times.  

This new analysis resulted in several additions to the Methods (see Section 2.5) and Results (see Tables 3 and 4). Overall, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the prefeedback baseline pupil and preceeding reaction time differences. There was only one difference to note between the correlation and linear mixed modeling analyses: for the error trials in the cue-target 2AFC task, including entropy in the model accounted for the variance previously explained by surprise. 

Reviewer #2 (Recommendations for the authors):

(1) Given the inherent temporal dependencies in pupil dynamics, characterising later pupil responses as independent of earlier ones in a three-way repeated measures ANOVA may not be appropriate. A more suitable approach might involve incorporating the earlier pupil response as a covariate in the model.

We thank the reviewer for bringing this issue to our attention. From our understanding, a repeated-measures ANOVA with factor “time window” would be appropriate in the current context for the following reasons. First, autocorrelation (closely tied to sphericity) is generally not considered a problem when only two timepoints are compared from time series data (Field, 2013; Tabachnick & Fidell, 2019). Second, the repeated-measures component of the ANOVA takes the correlated variance between time points into account in the statistical inference. Finally, as a complementary analysis, we present the results testing the interaction between the frequency and accuracy conditions across the full time courses (see Figures 1D and 2D); in these pupil time courses, any difference between the early and late time windows can be judged by the reader visually and qualitatively. 

(2) Please clarify the correlations between KL divergence, surprise, entropy, and pupil response time series. Specifically, state whether these correlations account for the interrelationships between these information-theoretic measures. Given their strong correlations, partialing out these effects is crucial for accurate interpretation.

As mentioned above, based on the suggestions by the reviewers we have included a complementary linear mixed model analysis in which we controlled for the effects of the information-theoretic variables on one another, while also including the nuisance regressors of pre-feedback baseline pupil dilation and reaction times.  

This new analysis resulted in several additions to the Methods (see Section 2.5) and Results (see Tables 3 and 4). Overall, the results of the linear mixed model corroborated the “simple” correlation analysis across the pupil time course while accounting for the relationship to the prefeedback baseline pupil and preceeding reaction time differences. There was only one difference to note between the correlation and linear mixed modeling analyses: for the error trials in the cue-target 2AFC task, including entropy in the model accounted for the variance previously explained by surprise. 

(3) The effects observed in the late time windows appear weak (e.g., Figure 2E vs. 2F, and the generally low correlation coefficients in Figure 3). Please elaborate on the reliability and potential implications of these findings.

We have now included a complementary linear mixed model analysis which also provides insight into the amount of explained variance of these information-theoretic predictors on the post-feedback pupil response, while also including the pre-feedback baseline pupil and reaction time differences (see section 3.3, Tables 3 & 4). The R² values ranged from 0.16 – 0.50 across all conditions tested. Including the pre-feedback baseline pupil dilation as a predictor in the linear mixed model analysis consistently led to more explained variance in the post-feedback pupil response, as expected.  

(4) In Figure 3 (C-J), please clarify how the trial-by-trial correlations were computed (averaged across trials or subjects). Also, specify how the standard error of the mean (SEM) was calculated (using the number of participants or trials).

The trial-by-trial correlations between the pupil signal and model parameters were computed for each participant, then the coefficients were averaged across participants for statistical inference. We have added several clarifications in the text (see section 2.5 and legends of Figure 3 and Supplementary Figure 4).

We have added “the standard error of the mean across participants” to all figure labels.

(5) For all time axes (e.g., Figure 2D), please label the ticks at 0, 0.5, 1, 1.5, 2, 2.5, and 3 seconds. Clearly indicate the duration of the feedback on the time axes. This is particularly important for interpreting the pupil dilation responses evoked by auditory feedback.

We have labeled the x-ticks every 0.5 seconds in all figures and indicated the duration of the auditory feedback in the letter-color decision task and as well as the stimuli presented in the control tasks in the Supplementary Materials. 

Reviewer #3 (Recommendations for the authors):

(1) Introduction page 3: "In information theory, information gain quantifies the reduction of uncertainty about a random variable given the knowledge of another variable. In other words, information gain measures how much knowing about one variable improves the prediction or understanding of another variable."

(2) In my opinion, the description of information gain can be clarified. Currently, it is not very concrete and quite abstract. I would recommend explaining it in the context of belief updating.

We have removed these unclear statements in the Introduction. We now clearly state the following:

“Information gain can be operationalized within information theory as the KullbackLeibler (KL) divergence between the posterior and prior belief distributions of a Bayesian observer, representing a formalized quantity that is used to update internal models [29,79,80].” (p. 4)

(3) Page 4: The inconsistencies across studies are described in extreme detail. I recommend shortening this part and summarizing the inconsistencies instead of listing all of the findings separately.

As per the reviewer’s recommendation, we have shortened this part of the introduction to summarize the inconsistencies in a more concise manner as follows: 

“Previous studies have shown different temporal response dynamics of prediction error signals in pupil dilation following feedback on decision outcome: While some studies suggest that the prediction error signals arise around the peak (~1 s) of the canonical impulse response function of the pupil [11,30,41,61,62,90], other studies have shown evidence that prediction error signals (also) arise considerably later with respect to feedback on choice outcome [10,25,32,41,62]. A relatively slower prediction error signal following feedback presentation may suggest deeper cognitive processing, increased cognitive load from sustained attention or ongoing uncertainty, or that the brain is integrating multiple sources of information before updating its internal model. Taken together, the literature on prediction error signals in pupil dilation following feedback on decision outcome does not converge to produce a consistent temporal signature.” (p. 5)

We would like to note some additional minor corrections to the preprint:

We have clarified the direction of the effect in Supplementary Figure 3 with the following: 

“Participants who showed a larger mean difference between the 80% as compared with the 20% frequency conditions in accuracy also showed smaller differences (a larger mean difference in magnitude in the negative direction) in pupil responses between frequency conditions (see Supplementary Figure 4).”

The y-axis labels in Supplementary Figure 3 were incorrect and have been corrected as the following: “Pupil responses (80-20%)”.

We corrected typos, formatting and grammatical mistakes when discovered during the revision process. Some minor changes were made to improve clarity. Of course, we include a version of the manuscript with Tracked Changes as instructed for consideration.

Author response:

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

Public Reviews:

Reviewer #1(Public review):

In this manuscript, Pagano and colleagues test the idea that the protein GMCL1 functions as a substrate receptor for a Cullin RING 3 E3 ubiquitin ligase (CUL3) complex. Using a pulldown approach, they identify GMCL1 binding proteins, including the DNA damage scaffolding protein 53BP1. They then focus on the idea that GMCL1 recruits 53BP1 for CUL3-dependent ubiquitination, triggering subsequent proteasomal degradation of ubiquitinated 53BP1.

In addition to its DNA damage signalling function, in mitosis, 53BP1 is reported to form a stopwatch complex with the deubiquitinating enzyme USP28 and the transcription factor p53 (PMID: 38547292). These 53BP1-stopwatch complexes generated in mitosis are inherited by G1 daughter cells and help promote p53-dependent cell cycle arrest independent from DNA damage (PMID: 38547292). Several studies show that knockout of 53BP1 overcomes G1 cell cycle arrest after mitotic delays caused by anti-mitotic drugs or centrosome ablation (PMID: 27432897, 27432896). In this model, it is crucial that 53BP1 remains stable in mitosis and more stopwatch complex is formed after delayed mitosis.

Major concerns:

Pagano and coworkers suggest that 53BP1 levels can sometimes be suppressed in mitosis if the cells overexpress GMCL1. They carry out a bioinformatic analysis of available public data for p53 wild-type cancer cell lines resistant to the anti-mitotic drug paclitaxel and related compounds. Stratifying GMCL1 into low and high expression groups reveals a weak (p = 0.05 or ns) correlation with sensitivity to taxanes. It is unclear on what basis the authors claim paclitaxel-resistant and p53 wild-type cancer cell lines bypass the mitotic surveillance/timer pathway. They have not tested this. Figure 3 is a correlation assembled from public databases but has no experimental tests. Figure 4 looks at proliferation but not cell cycle progression or the length of mitosis. The main conclusions relating to cell cycle progression and specifically the link to mitotic delays are therefore not supported by experimental data. There is no imaging of the cell cycle or cell fate after mitotic delays, or analysis of where the cells arrest in the cell cycle. Most of the cell lines used have been reported to lack a functional mitotic surveillance pathway in the recent work by Meitinger. To support these conclusions, the stability of endogenous 53BP1 under different conditions in cells known to have a functional mitotic surveillance pathway needs to be examined. A key suggestion in the work is that the level of GMCL1 expression correlates with resistance to taxanes. For the mitotic surveillance pathway, the type of drug (nocodazole, taxol, etc) used to induce a delay isn't thought to be relevant, only the length of the delay. Do GMCL1-overexpressing cells show resistance to anti-mitotics in general?

We thank the reviewer for this insightful comment. We propose that GMCL1 promotes CUL3-dependent ubiquitination of 53BP1 during prolonged mitotic arrest, thereby facilitating its proteasome-dependent degradation. To evaluate the potential clinical relevance of this mechanism, we stratified cancer cell lines based on GMCL1 mRNA expression using publicly available datasets from DepMap (PMID: 39468210). We observed correlations between GMCL1 expression levels and taxane sensitivity that appear to reflect specific cancer type-drug combinations. To experimentally evaluate this correlation and obtain mechanistic insights, we performed knockdown experiments in hTERT-RPE1 cells, which are known to possess an intact mitotic surveillance pathway. Silencing of GMCL1 alone inhibited cell proliferation and induced apoptosis, while co-depletion of either TP53BP1 or USP28 significantly rescued these effects. These results suggest that GMCL1 modulates the stability of 53BP1 and therefore the availability of the 53BP1-USP28-p53 ternary complex in cells with a functional mitotic surveillance pathway (MSP) (new Figure 5I,J) directly linking GMCL1 to the regulation of the MSP complex. Moreover, to further support our mechanism, we assessed the effect of GMCL1 levels on cell cycle progression. Briefly, following nocodazole synchronization and release, we treated cells with EdU and performed FACS analyses at different times. Knockdown of GMCL1 alone led to a delayed cell cycle progression, but co-depletion of either TP53BP1 or USP28 restored this phenotype (new Figure 3A and new Supplementary Figure 3A-C). These results are consistent with our proliferation data and suggest that the observed effects of GMCL1 are specific to mitotic exit. Finally, overexpression of GMCL1 accelerates cell cycle progression (as assessed by FACS analyses) upon release from prolonged mitotic arrest (new Figure 3B and new Supplementary Figure 3D-E). 

Importantly, if GMCL1 specifically degrades 53BP1 during prolonged mitotic arrests, the authors should show what happens during normal cell divisions without any delays or drug treatments. How much 53BP1 is destroyed in mitosis under those conditions? Does 53BP1 destruction depend on the length of mitosis, drug treatment, or does 53BP1 get degraded every mitosis regardless of length? Testing the contribution of key mitotic E3 ligase activities on mitotic 53BP1 stability, such as the anaphase-promoting complex/cyclosome (APC/C) is important in this regard. One previous study reported an analysis of putative APC/C KEN-box degron motifs in 53BP1 and concluded these play a role in 53BP1 stability in anaphase (PMID: 28228263).

Physiological mitosis under unperturbed conditions is typically brief (approximately 30 minutes), making protein quantification during this window challenging. Despite this, we tried by synchronizing cells using RO-3306 and releasing them into drug-free medium to assess GMCL1 dynamics during normal mitosis. Under these conditions, GMCL1 expression was similar to that in asynchronous cells and higher than the levels upon extended mitosis. However, when we attempted to measure the half-life of proteins using cycloheximide, most cells died, likely due to the toxic effect of cycloheximide in cells subjected to co-treatment with RO-3306 or nocodazole. This is the same reasons why in Figure 2C, we assessed 53BP1 in daughter cells rather than mitotic cells. 

There is no direct test of the proposed mechanism, and it is therefore unclear if 53BP1 is ubiquitinated by a GMCL1-CUL3 ligase in cells, and how efficient this process would be at different cell cycle stages. A key issue is the lack of experimental data explaining why the proposed mechanism would be restricted to mitosis. Indirect effects, such as loss of 53BP1 from the chromatin fraction during M phase upon GMCL1 overexpression, do not necessarily mean that 53BP1 is degraded. PLK1-dependent chromatin-cytoplasmic shuttling of 53BP1 during mitotic delays has been described previously (PMID: 38547292, 37888778). These papers are cited in the text, but the main conclusions of those papers on 53BP1 incorporation into a stopwatch complex during mitotic delays have been ignored. Are the authors sure that 53BP1 is destroyed in mitosis and not simply re-localised between chromatin and non-chromatin fractions? At the very least, these reported findings should be discussed in the text.

To examine whether GMCL1 promotes 53BP1 ubiquitination in cells, we expressed in cells Trypsin-Resistant Tandem Ubiquitin-Binding Entity (TR-TUBE), a protein that binds polyubiquitin chains. Abundant, endogenous ubiquitinated 53BP1 co-precipitated with TR-TUBE constructs only when wild-type GMCL1 but not the E142K GMCL1 mutant, was expressed (new Figure 2D).  The PLK1-dependent incorporation of 53BP1 into the stopwatch complex and the chromatin-cytoplasmic shuttling of 53BP1 during mitotic delays is now discussed in the text. That said, compared to parental cells, 53BP1 levels in the chromatin fraction are high in two different GMCL1 KO clones in M phase arrested cells (Figure 2A-B).  This increase does not correspond to a decrease in the 53BP1 soluble fraction (Figure 2A and new Supplementary Figure 2D), suggesting decreased 53BP1 is not due to re-localization. The increased half-life of 53BP1 in daughter cells (Figure 2C), also supports this hypothesis. 

The authors use a variety of cancer cell line models throughout their study, most of which have been reported to lack a functional mitotic surveillance pathway. U2OS and HCT116 cells do not respond normally to mitotic delays, despite being annotated as p53 WT. Other studies have used p53 wild-type hTERT RPE-1 cells to study the mitotic surveillance pathway. If the model is correct, then over-expressing GMCL1 in hTERT-RPE1 cells should suppress cell cycle arrest after mitotic delays, and GMCL1 KO should make the cells more sensitive to delays. These experiments are needed to provide an adequate test of the proposed model.

We greatly appreciate the reviewer’s suggestion regarding overexpression of GMCL1 in hTERT-RPE1 cells. To address this, we generated stable RPE1 cells expressing V5-tagged GMCL1 and conducted EdU incorporation assays following nocodazole synchronization and release. Overexpression of GMCL1 enhanced cell cycle progression compared to control cells (new Figure 3B and new Supplementary Figure 3D-E) after mitotic arrest, consistent with our model. We, therefore, propose that GMCL1 controls 53BP1 stability to suppress p53-dependent cell cycle arrest.

We also want to point out that while some papers suggest that HCT116 and U2OS cells do not have an intact mitotic surveillance pathway, others have shown that the MSP is indeed functioning in HCT116 cells and can be triggered with variable efficiency in U2OS cells (PMID: 38547292). This is likely due to high heterogeneity and extensive clonal diversity of cancer cell lines grown in different labs. Please see examples in PMIDs: 3620713, 30089904, and 30778230. In particular, PMID: 30089904 shows that this heterogeneity correlates with considerably different drug responses. 

To conclude, while the authors propose a potentially interesting model on how GMCL1 overexpression could regulate 53BP1 stability to limit p53-dependent cell cycle arrest, it is unclear what triggers this pathway or when it is relevant. 53BP1 is known to function in DNA damage signalling, and GMCL1 might be relevant in that context. The manuscript contains the initial description of GMCL1-53BP1 interaction but lacks a proper analysis of the function of this interaction and is therefore a preliminary report.

We hope that the new experiments, along with the clarifications provided in this response letter and revised manuscript, offer the reviewer increased confidence in the robustness and validity of our proposed model.

Reviewer #2 (Public review):

This study investigates the role of GMCL1 in regulating the mitotic surveillance pathway (MSP), a protective mechanism that activates p53 following prolonged mitosis. The authors identify a physical interaction between 53BP1 and GMCL1, but not with GMCL2. They propose that the ubiquitin ligase complex CRL3-GMCL1 targets 53BP1 for degradation during mitosis, thereby preventing the formation of the "mitotic stopwatch" complex (53BP1-USP28-p53) and subsequent p53 activation. The authors show that high GMCL1 expression correlates with resistance to paclitaxel in cancer cell lines that express wild-type p53. Importantly, loss of GMCL1 restores paclitaxel sensitivity in these cells, but not in p53-deficient lines. They propose that GMCL1 overexpression enables cancer cells to bypass MSP-mediated p53 activation, promoting survival despite mitotic stress. Targeting GMCL1 may thus represent a therapeutic strategy to re-sensitize resistant tumors to taxane-based chemotherapy.

Strengths:

This manuscript presents potentially interesting observations. The major strength of this article is the identification of GMCL1 as a 53BP1 interaction partner. The authors identified relevant domains and showed that GMCL1 controls 53BP1 stability. The authors further show a potentially interesting link between GMCL1 status and sensitivity to Taxol.

Weaknesses:

However, the manuscript is significantly weakened by unsubstantiated mechanistic claims, overreliance on a non-functional model system (U2OS), and overinterpretation of correlative data. To support the conclusions of the manuscript, the authors must show that the GMCL1-dependent sensitivity to Taxol depends on the mitotic surveillance pathway.

To demonstrate that GMCL1-dependent taxane sensitivity is mediated through the mitotic surveillance pathway (MSP), we now performed experiments using hTERT-RPE1 (RPE1) cells, a widely used, non-transformed cell line known to possess a functional MSP.  We compared RPE1 cells with knockdown of GMCL1 alone to those with simultaneous knockdown of GMCL1 and either TP53BP1 or USP28. Upon paclitaxel (Taxol) treatment, cells with GMCL1 knockdown exhibited suppressed proliferation and increased apoptosis. Notably, these phenotypes were rescued by co-depletion of TP53BP1 or USP28 (new Figure 5I,J). These results support the notion that GMCL1 contributes to MSP activity, at least in part, through its regulation of 53BP1.       

To further strengthen our mechanistic experiments, we assessed the effect of GMCL1 levels on cell cycle progression. Following nocodazole synchronization and release, we treated cells with EdU and performed FACS analyses at different times. Knockdown of GMCL1 alone led to a delay in cell cycle progression, but co-depletion of either TP53BP1 or USP28 alleviate this phenotype (new Figure 3A and new Supplementary Figure 3A, B). These results are consistent with our proliferation data.

Reviewer #3 (Public review):

Summary:

In this study, Kito et al follow up on previous work that identified Drosophila GCL as a mitotic substrate recognition subunit of a CUL3-RING ubiquitin ligase (CRL3) complex.

Here they characterize mutants of the human ortholog of GCL, GMCL1, that disrupt the interaction with CUL3 (GMCL1E142K) and that lack the substrate interaction domain (GMCL1 BBO). Immunoprecipitation followed by mass spectrometry identified 9 proteins that interacted with wild-type FLAG-GMCL1 and GMCL1 EK but not GMCL1 BBO. These proteins included 53BP1, which plays a well-characterized role in double-strand break repair but also functions in a USP28-p53-53BP1 "mitotic stopwatch" complex that arrests the cell cycle after a substantially prolonged mitosis. Consistent with the IP-MS results, FLAG-GMCL1 immunoprecipitated 53BP1. Depletion of GMCL1 during mitotic arrest increased protein levels of 53BP1, and this could be rescued by wild-type GMCL1 but not the E142K mutant or a R433A mutant that failed to immunoprecipitate 53BP1.

Using a publicly available dataset, the authors identified a relatively small subset of cell lines with high levels of GMCL1 mRNA that were resistant to the taxanes paclitaxel, cabazitaxel, and docetaxel. This type of analysis is confounded by the fact that paclitaxel and other microtubule poisons accumulate to substantially different levels in various cell lines (DOI: 10.1073/pnas.90.20.9552 , DOI: 10.1091/mbc.10.4.947 ), so careful follow-up experiments are required to validate results. The correlation between increased GMCL1 mRNA and taxane resistance was not observed in lung cancer cell lines. The authors propose this was because nearly half of lung cancers harbor p53 mutations, and lung cancer cell lines with wild-type but not mutant p53 showed the correlation between increased GMCL1 mRNA and taxane resistance. However, the other cancer cell types in which they report increased GMCL1 expression correlates with taxane sensitivity also have high rates of p53 mutation. Furthermore, p53 status does not predict taxane response in patients (DOI: 10.1002/1097-0142(20000815)89:4<769::aid-cncr8>3.0.co;2-6 , DOI: 10.1002/(SICI)1097-0142(19960915)78:6<1203::AID-CNCR6>3.0.CO;2-A , PMID: 10955790).

The authors then depleted GMCL1 and reported that it increased apoptosis in two cell lines with wild-type p53 (MCF7 and U2OS) due to activation of the mitotic stopwatch. This is surprising because the mitotic stopwatch paper they cite (DOI: 10.1126/science.add9528 ) reported that U2OS cells have an inactive stopwatch and that activation of the stopwatch results in cell cycle arrest rather than apoptosis in most cell types, including MCF7. Beyond this, it has recently been shown that the level of taxanes and other microtubule poisons achieved in patient tumors is too low to induce mitotic arrest (DOI: 10.1126/scitranslmed.3007965 , DOI: 10.1126/scitranslmed.abd4811 , DOI: 10.1371/journal.pbio.3002339 ), raising concerns about the relevance of prolonged mitosis to paclitaxel response in cancer. The findings here demonstrating that GMCL1 mediates degradation of 53BP1 during mitotic arrest are solid and of interest to cell biologists, but it is unclear that these findings are relevant to paclitaxel response in patients.

Strengths:

This study identified 53BP1 as a target of CRL3GMCL1-mediated degradation during mitotic arrest. AlphaFold3 predictions of the binding interface, followed by mutational analysis, identified mutants of each protein (GMCL1 R433A and 53BP1 IEDI1422-1425AAAA) that disrupted their interaction. Knock-in of a FLAG tag into the C-terminus of GMCL1 in HCT116 cells, followed by FLAG immunoprecipitation, confirmed that endogenous GMCL1 interacts with endogenous CUL3 and 53BP1 during mitotic arrest.

Weaknesses:

The clinical relevance of the study is overinterpreted. The authors have not taken relevant data about the clinical mechanism of taxanes into account. Supraphysiologic doses of microtubule poisons cause mitotic arrest and can activate the mitotic stopwatch. However, in physiologic concentrations of clinically useful microtubule poisons, cells proceed through mitosis and divide their chromosomes on mitotic spindles that are at least transiently multipolar. Though these low concentrations may result in a brief mitotic delay, it is substantially shorter than the arrest caused by high concentrations of microtubule poisons, and the one mimicked here by 16 hours of 0.4 mg/mL nocodazole, which is not used clinically and does not induce multipolar spindles. Resistance to mitotic arrest occurs through different mechanisms than resistance to multipolar spindles. No evidence is presented in the current version of the manuscript that GMCL1 affects cellular response to clinically relevant doses of paclitaxel.

We agree that it would be an overstatement to claim that GMCL1 and p53 regulates paclitaxel sensitivity in cancer patients in a clinical context. The correlations we observed were based on publicly available cancer cell lines from datasets catalogued in CCLE and DepMap, which do not fully account for clinical heterogeneity and patient-specific factors. In response to this important point, we have revised the text accordingly. 

In the experiments shown in former Figure 4A-H (now Figure 5A-H) and in those shown in the new Figure 5I-J, we used 100 nM paclitaxel to test the hypothesis that low GMCL1 levels sensitizes cancer cells in a p53-dependent manner. Here, paclitaxel was chosen to mimic the conditions reported in the PRISM dataset (PMID: 32613204), which compiles the proliferation inhibitory activity of 4,518 compounds tested across 578 cancer cell lines. Consistent with our cell cycle findings, the paclitaxel sensitivity caused by GMCL1 depletion was reverted by silencing 53BP1 or USP28 (new Figure 5I-J), again supporting the involvement of the stopwatch complex. We are unsure about how to model the “physiologic concentrations of clinically useful microtubule poisons” in cell-based studies. A recent review notes that “The time above a threshold paclitaxel plasma concentration (0.05 mmol/L) is important for the efficacy and toxicity of the drug” (PMID: 28612269).  Two other reviews mention that the clinically relevant concentration of paclitaxel is considered to be plasma levels between 0.05–0.1 μmol/L (approximately 50–100 nM) and that in clinical dosing, typical patient plasma concentrations after paclitaxel infusion range from 80–280 nM, with corresponding intratumoral concentrations between 1.1–9.0 μM, due to drug accumulation in tumor tissue (PMIDs: 24670687 and  29703818).  We have now emphasized in the revised text the rationale for using 100 nM paclitaxel in our experiments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

General comments on the Figures:

(1) Western blots lack molecular weight markers on most panels and are often over-exposed and over-contrasted, rendering them hard to interpret.

We have now included molecular weight markers in all Western blot panels. We have also reprocessed the images to avoid overexposure and excessive contrast, ensuring that the bands are clearly visible and interpretable.

(2) Input and IP samples do not show percentage loading, so it is hard to interpret relative enrichments.

In the revised figures, we have indicated what % of the input was loaded.

(3) The authors change between cell line models for their experiments, and this is not clear in the figures. These are important details for interpreting the data, as many of the cell lines used are not functional for the mitotic surveillance pathway.

In the revised manuscript, we have clearly indicated the specific cell lines used in each experiment in the figure legends. Additionally, to address concerns regarding the mitotic surveillance pathway, we have included new experiments using hTERT-RPE1 cells, which have been reported to possess a functional mitotic surveillance pathway (MSP) (Figure 4I-J).

(4) No n-numbers are provided in the figure legends. Are the Western blots provided done once, or are they reproducible? Many of the blots would benefit from quantification and presentation via graphs to test for reproducible changes to 53BP1 levels under the different conditions.

As now indicated in the methods section, we have conducted each Western blot no less than three times, yielding results that exhibit a high degree of reproducibility. A representative Western blot has been selected for each figure. We did not include densiometric quantification of immunoblots, given that the semi-quantitative nature of this technique would lead to an overinterpretation of our data; unfortunately, this is a limitation of the technique. In fact, eLife and other similar scientific journals do not adhere to the practice of quantifying Western blots. One exception to this norm is for protein half-life studies, which is done to measure the kinetics of decay rates and their internal comparisons. Accordingly, the experiments in Figure 2C were quantified.

(5) Graphs displayed in the supplementary figures are blacked out, and individual data points cannot be visualised. All graphs should have individual data points clearly visible.

We revised the quantified graphs and replaced them with scatter plots to clearly display individual data points, showing sample distribution.

Additional experiments with specific comments on Figures:

(1) Figure 1C-D: the relative amount of 53BP1 co-precipitating with FLAG-tagged GMCL1 WT appears very different between the two experiments. If the idea is that MLN4924 (Cullin neddylation inhibitor) makes the interaction easier to capture, then this should be explained in the text, and ideally shown on the same gel/blot -/+ MLN4924.

We now present the samples treated with and without MLN4924 on the same gel/blot to allow direct comparison (new Figure 1D) and clarified this point in the text.

(2) Figure 1E: The figure legend states that GMCL1 was immunoprecipitated, but the Figure looks as though FLAG-tagged 53BP1 was the bait protein being immunoprecipitated? Can the authors clarify?

We thank the reviewer for pointing out the discrepancy between the figure and the figure legend in Figure 1E. The immunoprecipitation was indeed performed using FLAG-tagged 53BP1, and we have now rectified the figure legend accordingly. 

(3) Figure 1F: Rather than parental cell lysate, the better control would be to IP FLAG from another FLAG-tagged expressing cell line, to rule out non-specific binding with the FLAG tag at the non-overexpressed level. 

Figure 1F shows interaction at the endogenous level. The specificity of binding with overexpressed proteins is shown in Figures 1C and 1D.

The USP28 blot is over-exposed and makes it hard to see any changes in electrophoretic mobility - it looks as though there is a change between the parental and the KI cell line? It is surprising that USP28 would co-IP with GMCL1 (presumably because USP28 is bound to 53BP1) if the function of GMCL1-53BP1 interaction is to promote 53BP1 degradation. Can the authors reconcile this? Crucially, if the authors claim that the 53BP1-GMCL1 interaction is specific to prolonged mitosis, then this experiment should be repeated and performed with asynchronous, normal-length mitosis, and prolonged mitosis conditions. This is vital for supporting the claim that this interaction only occurs during prolonged mitoses and does not occur in every mitosis regardless of length.

This is a good point. Unfortunately, many of the protein-protein interactions occur post lysis. Therefore, we could not observe differences in asynchronous vs. mitotic cells.

(4) Figure S1F: Label on blot should be CUL3 not CUI3.

We thank the reviewer for pointing this out and we have corrected the typo.

(5) Figure 2A: The authors suggest an increase in chromatin-bound 53BP1 in GMCL1 KO U2OS cells, specifically in M phase. Again, is this time in mitosis dependent, or would this be evident in every mitosis, regardless of length? Such an experiment would benefit from repetition and quantification to test whether the observed effect is reproducibly consistent. If the authors' model is correct, simply treating U2OS WT mitotic cells with MG132 during the mitotic arrest and performing the same fractionation should bring 53BP1 levels up to that seen in GMCL1 KO cells under the same conditions.

The reviewer’s suggestion to assess 53BP1 accumulation in wild-type U2OS cells treated with MG132 during mitotic arrest is indeed highly relevant. However, treatment with MG132 during prolonged mitosis consistently led to significant cell death, making it technically challenging to evaluate 53BP1 levels under these conditions.

(6) Figure 2B: The authors restore GMCL1 expression in the KO U2OS cells using WT and 2 distinct mutant cDNAs. However, the expression of these constructs is not equivalent, and thus their effects cannot be directly compared. It is also surprising that GMCL1 is much higher in M phase samples in this experiment (shouldn't it be destroyed?), when no such behaviour has been observed in the other figures.

There is no evidence in our study or others that GMCL1 should be destroyed in M phase.  We show that the R433A mutant is expressed at a level very similar to the WT protein, yet it doesn’t promote the degradation of 53BP1. It is true that the E142K is expressed less in mitotic cells whereas is the most expressed in asynchronous cells. For some reason, this mutant has an inverse behavior compared to the WT, limiting the interpretation of this result. We now mention this in the text. 

(7) Figure 2C: The CHX experiment would benefit from inclusion of a control protein known to have a short half-life (e.g. c-myc, p53). Is GMCL1 known to have a relatively short half-life? It looks as though GMCL1 disappears after 1 h CHX treatment (although hard to definitively tell in the absence of molecular weight markers). 53BP1 appears to continue declining in the absence of GMCL1, which is surprising if p53BP1 degradation requires GMCL1. How can the authors reconcile this?

As a control for the CHX chase experiments, we included p21, whose protein levels decreased in a CHX-dependent. GMCL1 itself also appeared to undergo degradation upon CHX treatment, but it doesn’t disappear completely.

(8) Supplemental Figure 2:

Transcription is largely inhibited in M phase, so the p53 target gene transcripts present in M phase are inherited from the preceding G2 phase. The qPCR's thus need a reference sample to compare against. I.e., was p21/PUMA/NOXA mRNA already low in G2 in the GMCL1 KO + WT cells before they entered mitosis? Or is the mRNA stability affected during M phase specifically? Is this effect on the mRNA dependent on the time in mitosis?

It is well established that transcription is not entirely shut down during mitosis, particularly for a subset of genes involved in cell cycle regulation. For example, p21, PUMA, NOXA, and p53 mRNAs have been shown to remain actively transcribed during mitosis (see Table S5 in PMID: 28912132). However, we currently lack direct evidence that p53 activation during mitosis, specifically through the mitotic surveillance pathway, drives the transcription of p21, PUMA, or NOXA mRNAs during M phase. In the absence of such mechanistic data, we opted to exclude these analyses from the final figures.

Panel B: blots are too over-exposed to see differences in p53 stability under the different conditions. Mitotic samples should be included to show how these differ from the G1 samples.

The background of all blot images has been adjusted to ensure clarity and consistency.

Panel D: The authors show no significant difference in the cell cycle profiles of the GMCL1 KO and reconstituted cells compared to parental U2OS cells. This should also be performed in the G1 daughter cells following a prolonged mitosis, to test the effect of the different GMCL1 constructs on G1 cell cycle arrest. U2OS cells have been reported not to have a functional mitotic surveillance pathway (Meitinger et al, Science, 2024), so U2OS cells are perhaps not a good model for testing this.

We performed cell cycle profiling using EdU incorporation in hTERT-RPE1 cells, which possess a functional MSP, to evaluate cell cycle progression in daughter cells following prolonged mitosis. We observed that GMCL1 knockdown alone leads to G1-phase arrest. In contrast, co-depletion of GMCL1 with either 53BP1 or USP28 bypasses this arrest, indicating that GMCL1 regulates cell cycle progression in an MSP-dependent manner. Please see also the answer to the public review above. 

(9) Figure 3:

The authors show expression data for GMCL1 in the different cancer cell lines. This should be validated for a subset of cancer cell lines at the GMCL1 protein level, and cross-correlated to their MSP/mitotic timer status. Does GMCL1 depletion or knockout in p53 wild-type cancer cell lines overexpressing GMCL1 protein restore mitotic surveillance function?

We were unable to assess GMCL1 protein levels using publicly available proteomics datasets, as GMCL1 expression was not detected. In p53 wild-type hTERT-RPE1 cells, GMCL1 knockdown impaired the mitotic surveillance pathway, as evidenced by G1-phase arrest following prolonged mitosis (new Figure 3A and new Supplementary Figure 3A, B). This arrest was rescued by co-depletion of either TP53BP1 or USP28, indicating that GMCL1 acts upstream of the MSP.

(10) Figure 4:

The authors show siRNA experiments depleting GMCL1 and testing the effects of GMCL1 loss on cell viability and apoptosis induction. This is performed in different cell line backgrounds. However, there is no demonstration that any of the observed effects are due to a lack of GMCL1 activity on 53BP1. These experiments need to be repeated in 53BP1 co-depleted cells to test for rescue. Without this, the interpretation is purely correlative.

We assessed the effects of GMCL1 knockdown, alone or in combination with TP53BP1 or USP28 knockdown, on cell viability and apoptosis in hTERT-RPE1 cells using siRNA. Knockdown of GMCL1 alone led to a significant reduction in cell viability and an increase in apoptosis. However, co-depletion of GMCL1 with either TP53BP1 or USP28 restored both cell viability and apoptosis levels to those observed in control cells (new Figure 5I,J).

(11) Text comments:

Line 257: HeLa cells supress p53 through the E6 viral protein and are not "mutant" for p53.

The authors should cite early work by Uetake and Sluder describing the effects of spindle poisons on the mitotic surveillance pathway.

We appreciate the reviewer’s comments – We have now made the necessary corrections.

Reviewer #2 (Recommendations for the authors):

Major Points:

(1) Unsubstantiated Mechanistic Claims:

In Figures 3 and 4, the authors show correlations between GMCL1 expression and sensitivity to Taxol. However, they fail to demonstrate that the mitotic stopwatch is mechanistically involved. To support this conclusion, the authors must test whether deletion of 53BP1, USP28, or disruption of their interaction rescues Taxol sensitivity in GMCL1-depleted cells. Since 53BP1 also plays a role in DNA damage response, such rescue experiments are necessary to distinguish between mitotic surveillance-specific and broader stress-response effects. Deletion of USP28 would be particularly informative.

We sought to experimentally determine whether GMCL1 is involved in regulating the mitotic stopwatch. Knockdown of GMCL1 alone resulted in reduced cell proliferation and increased apoptosis. In contrast, co-depletion of GMCL1 with either TP53BP1 or USP28 restored both proliferation and apoptosis levels to those observed in control cells (new Figure 5I, J). To further strengthen our mechanistic experiments, we assessed the effect of GMCL1 levels on cell cycle progression. We conducted EdU incorporation assays following nocodazole synchronization and release. Knockdown of GMCL1 alone led to a delay in G1 progression, whereas co-depletion of either TP53BP1 or USP28 rescued normal cell cycle progression (new Figure 3A and new Supplementary Figure 3A, B). These results are consistent with our proliferation data and suggest that GMCL1 functions upstream of the ternary complex, likely by regulating 53BP1 protein levels.

(2) Model System Limitations (U2OS Cells):

The use of U2OS cells is highly problematic for investigating the mitotic surveillance pathway. U2OS cells lack a functional mitotic stopwatch and do not arrest following prolonged mitosis in a 53BP1/USP28-dependent manner (PMID: 38547292). Therefore, conclusions drawn from this model system about the function of the mitotic surveillance pathway are not substantiated. Key experiments should be repeated in a cell line with an intact pathway, such as RPE1.

We now performed all key experiments also hTERT-RPE1 cells (see above). We also would like to point out that while some papers suggest that HCT116 and U2OS cells do not have an intact mitotic surveillance pathway, others have showed that the MSP is indeed functioning in HCT116 cells and can be triggered with variable efficiency in U2OS cells (PMID: 38547292).  This is likely due to high heterogeneity and extensive clonal diversity of cancer cell lines grown in different labs. Please see examples in PMIDs: 3620713, 30089904, and 30778230. In particular, PMID: 30089904 shows that this heterogeneity correlates with considerably different drug responses. 

(3) Misinterpretation of p53 Activity Timing:

The manuscript states that "GMCL1 KO cells led to decreased mRNA levels of p21 and NOXA during mitosis" (line 194). However, it is well established that the mitotic surveillance pathway activates p53 in the G1 phase following prolonged mitosis-not during mitosis itself (PMID: 38547292). Therefore, the observed changes in mRNA levels during mitosis are unlikely to be relevant to this pathway.

We currently lack direct evidence that p53 activated during mitosis through the mitotic surveillance pathway directly influences the transcription of p21, PUMA, or NOXA mRNAs during M phase. Therefore, we have chosen to exclude these data from the final figures.

(4) Incorrect Interpretation of 53BP1 Chromatin Binding:

The authors claim that 53BP1 remains associated with chromatin during mitosis, which contradicts established literature. It is known that 53BP1 is released from chromatin during mitosis via mitosis-specific phosphorylation (PMID: 24703952), and this is supported by more recent findings (PMID: 38547292). A likely explanation for the discrepancy may be contamination of mitotic fractions with interphase cells. The chromatin fraction data in Figure 2C must be interpreted with caution.

Our method to synchronize in M phase is rather stringent (see Supplementary Figure 3D as an example). The literature indicates that the bulk of 53BP1 is released from chromatin during mitosis. Yet, even in the two publications mentioned by the reviewer, there is a difference in the observable amount of 53BP1 bound to chromatin (compare Figure 2B in PMID: 38547292 and Figure 5A in PMID: 24703952). The difference is likely due to the different biochemical approaches used to purify chromatin bound proteins (salt and detergent concentrations, sonication, etc.). Using our fractionation approach, we can reliably separate the soluble fraction (containing also the nucleoplasmic fraction) and chromatin associated proteins as indicated by the controls such as a-Tubulin and Histon H3.  We have now mentioned these limitations when comparing different fractionation methods in our discussion section.

(5) Inadequate Citation of Foundational Literature:

The literature on the mitotic surveillance pathway is relatively limited, and it is essential that the authors provide a comprehensive and accurate account of its development. The foundational work by the Sluder lab (PMID: 20832310), demonstrating a p53-dependent arrest following prolonged mitosis, must be cited. Furthermore, the three key 2016 papers (PMID: 27432896, 27432897, 27432896) that identified the involvement of USP28 and 53BP1 in this pathway are critical and should be cited as the basis of the mitotic surveillance pathway.

In contrast, the manuscript currently emphasizes publications that either contribute minimally or have been contradicted by prior and subsequent work. For example: PMID: 31699974, which proposes Ser15 phosphorylation of p53 as critical, has been contradicted by multiple groups (e.g., Holland, Oegema, and Tsou labs).

PMID: 37888778, which suggests that 53BP1 must be released from kinetochores, is inconsistent with findings that indicate kinetochore localization is not relevant.

The authors should thoroughly revise the Introduction to reflect what this reviewer would describe as a more accurate and scholarly approach to the literature.

We have substantially revised both the Introduction and Discussion sections to incorporate important references kindly suggested by the reviewer.

Minor Points:

(1) Overexposed Western Blots:

The Western blots throughout the manuscript are heavily overexposed and saturated, obscuring differences in protein levels and hindering data interpretation. The authors should provide properly exposed blots with quantification where appropriate.

We have provided Western blot images with appropriate exposure levels and included quantification where appropriate (i.e., to measure the kinetics of decay rates as in Figure 2C). For all the other immunoblots, we did not include densiometric quantification, given that the semi-quantitative nature of this technique would lead to overinterpretation of our data. This is, unfortunately, a limitation of the technique. In fact, eLife and other similar scientific journals do not adhere to the practice of quantifying Western blot analyses. 

(2) Missing information in the graphs in Figure 2C and 4; S2? How many repeats? What are the asterisks?

Panels referenced above have been repeated several times, and further details are now provided in the figure legends.

Reviewer #3 (Recommendations for the authors):

(1)   The claim that GMCL1 modulates paclitaxel sensitivity in cancer should be toned down

.

We agree that it would be an overstatement to claim that GMCL1 regulates paclitaxel sensitivity in cancer patients in a clinical context. The correlations we observed were based on publicly available, cell line–based datasets, which do not fully account for clinical heterogeneity and patient-specific factors. In response to this important point, we have revised our statements and corresponding text accordingly. We now placed greater emphasis on our molecular and cell biology studies.

(2) Additional experiments in low, physiologically relevant concentrations of paclitaxel would be interesting. It is possible that these concentrations activate the mitotic stopwatch in a portion of cells, in addition to inducing cell death due to chromosome loss, activation of an immune response, and chromothripsis. Results should be interpreted in the context of this complexity.

Please see the response to the public review. 

(3) It would be helpful to show that CUL3 interacts with 53BP1 only in the presence of GMCL1.

We show that the binding of 53BP1 to GMCL1 is independent of the ability of GMCL1 to bind CUL3 (Figure 1C, D). The binding between 53BP1 and CUL3 is difficult to detect (Figure 1F) likely because it’s not direct but mediated by GMCL1.

(4) The GMCL1 "KO" lines appear to still express a low level of GMCL1 (Figure 2A), which should be acknowledged

We have included the GMCL1 mRNA expression data, as measured by RT-PCR, in Supplementary Figure 1G, demonstrating that GMCL1 expression was undetectable under the tested conditions.

(5) Additional description of the methods is warranted. This is particularly true for the database analysis that forms the basis for the claim that GMCL1 overexpression causes resistance to paclitaxel and other taxanes presented in Figure 3, the methodology used to obtain M-phase cells, and the concentration and duration of taxol treatment.

We have now extensively revised the Methods section.  

(6) "Taxol" and "paclitaxel" are used interchangeably throughout the manuscript. Consistency would be preferable.

We have revised the manuscript to maintain consistency in the use of the terms “Taxol” and “paclitaxel” and now refer to “paclitaxel” when discussing that individual compound; “taxanes” when referring collectively to cabazitaxel, docetaxel and paclitaxel; and “Taxol” has been removed entirely to avoid redundancy or confusion.    

(7) It is unclear why it is claimed that GMCL1 interacts "specifically" with 53BP1 (line 176) since multiple interactors were identified in the IP-MS study

We meant that the GMCL1 R433A mutant loses its ability to bind 53BP1, suggesting that the GMCL1-53BP1 interaction is not an artifact. We have now clarified the text. 

(8) The bottom row in Figure S3 is misleading. Paclitaxel is not uniformly effective in every tumor of any given type, and so resistance occurs in every cancer type.

We fully agree that cancer is highly heterogeneous and that paclitaxel efficacy varies across tumors, even within the same histological subtype. Our intension was not to suggest uniform sensitivity/resistance, but rather to provide a high-level overview using aggregated data. We acknowledge that this coarse-grained representation may unintentionally imply overly generalized conclusions. To avoid potential misinterpretation, we have removed the corresponding panel in the revised paper.

Author response:

Here we provide a provisional response addressing the public comments and outlining the revisions we are planning to make:

(1) We will add additional baseline models to delineate the contributions of the acoustic and linguistic pathways.

(2) We will show additional ablation analysis and other model comparison results, as suggested by the reviewers, to justify the choice of the DNN models.

(3) We will clarify the use of the TIMIT dataset during pre-training. In fact, the TIMIT speech data (the speech corpora used in the test set) was not included or used when pre-training the acoustic or linguistic pathway. It was only used in fine-tuning the final speech synthesizer (the cosyvoice model). We will present results without this fine-tuning step, which will fully eliminate the usage of the TIMIT data during model training.

(4) We will further analyze the phoneme confusion matrices and/or other data to evaluate the model behavior.

(5) We will analyze the test sentences with high and low accuracies. We will also include results with partial training data (e.g. using 25%, 50%, 75% of the training set) to further evaluate the impact of the total amount of training data.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This research group has consistently performed cutting-edge research aiming to understand the role of hormones in the control of social behaviors, specifically by utilizing the genetically-tractable teleost fish, medaka, and the current work is no exception. The overall claim they make, that estrogens modulate social behaviors in males and females is supported, with important caveats. For one, there is no evidence these estrogens are generated by "neurons" as would be assumed by their main claim that it is NEUROestrogens that drive this effect. While indeed the aromatase they have investigated is expressed solely in the brain, in most teleosts, brain aromatase is only present in glial cells (astrocytes, radial glia). The authors should change this description so as not to mislead the reader. Below I detail more specific strengths and weaknesses of this manuscript.

We thank the reviewer for this positive evaluation of our work and for the helpful comments and suggestions. Regarding the concern that the term “neuroestrogens” may be misleading, we addressed this in the previous revision by consistently replacing it throughout the manuscript with “brain-derived estrogens” or “brain estrogens.”

In addition, the following sentence was added to the Introduction (line 61): “In teleost brains, including those of medaka, aromatase is exclusively localized in radial glial cells, in contrast to its neuronal localization in rodent brains (Forlano et al., 2001; Diotel et al., 2010; Takeuchi and Okubo, 2013).”

Strenghth:

Excellent use of the medaka model to disentangle the control of social behavior by sex steroid hormones 

The findings are strong for the most part because deficits in the mutants are restored by the molecule (estrogens) that was no longer present due to the mutation 

Presentation of the approach and findings are clear, allowing the reader to make their own inferences and compare them with the authors' 

Includes multiple follow-up experiments, which leads to tests of internal replication and an impactful mechanistic proposal 

Findings are provocative not just for teleost researchers, but for other species since, as the authors point out, the data suggest mechanisms of estrogenic control of social behaviors may be evolutionary ancient 

We thank the reviewer again for their positive evaluation of our work.

Weakness:

As stated in the summary, the authors are attributing the estrogen source to neurons and there isn't evidence this is the case. The impact of the findings doesn't rest on this either

As mentioned above, we addressed this in the previous revision by replacing “neuroestrogens” with “brain-derived estrogens” or “brain estrogens” throughout the manuscript. In addition, the following sentence was added to the Introduction (line 61): “In teleost brains, including those of medaka, aromatase is exclusively localized in radial glial cells, in contrast to its neuronal localization in rodent brains (Forlano et al., 2001; Diotel et al., 2010; Takeuchi and Okubo, 2013).”

The d4 versus d8 esr2a mutants showed different results for aggression. The meaning and implications of this finding are not discussed, leaving the reader wondering

This comment is the same as one raised in the first review (Reviewer #1’s comment 2 on weaknesses), which we already addressed in our initial revision. For the reviewer’s convenience, we provide the response below:

Line 300: As the reviewer correctly noted, circles were significantly reduced in mutant males of the Δ8 line, whereas no significant reduction was observed in those of the Δ4 line. However, a tendency toward reduction was evident in the Δ4 line (P = 0.1512), and both lines showed significant differences in fin displays. Based on these findings, we believe our conclusion that esr2a^−/− males exhibit reduced aggression remains valid. To clarify this point and address potential reader concerns, we have revised the text as follows: “esr2a^−/− males exhibited significantly fewer fin displays (P = 0.0461 and 0.0293 for Δ8 and Δ4 lines, respectively) and circles (P = 0.0446 and 0.1512 for Δ8 and Δ4 lines, respectively) than their wild-type siblings (Fig. 5L; Fig. S8E), suggesting less aggression” was edited to read “esr2a^−/− males from both the Δ8 and Δ4 lines exhibited significantly fewer fin displays than their wild-type siblings (P = 0.0461 and 0.0293, respectively). Circles followed a similar pattern, with a significant reduction in the Δ8 line (P = 0.0446) and a comparable but non-significant decrease in the Δ4 line (P =0.1512) (Figure 5L, Figure 5—figure supplement 3E), showing less aggression.”

Lack of attribution of previous published work from other research groups that would provide the proper context of the present study

This comment is also the same as one raised in the first review (Reviewer #1’s comment 3 on weaknesses). In our previous revision, in response to this comment, we cited the relevant references (Hallgren et al., 2006; O’Connell and Hofmann, 2012; Huffman et al., 2013; Jalabert et al., 2015; Yong et al., 2017; Alward et al., 2020; Ogino et al., 2023) in the appropriate sections. We also added the following new references and revised the Introduction and Discussion accordingly:

(2) Alward BA, Laud VA, Skalnik CJ, York RA, Juntti SA, Fernald RD. 2020. Modular genetic control of social status in a cichlid fish. Proceedings of the National Academy of Sciences of the United States of America 117:28167–28174. DOI: https://doi.org/10.1073/pnas.2008925117

(39) O’Connell LA, Hofmann HA. 2012. Social status predicts how sex steroid receptors regulate complex behavior across levels of biological organization. Endocrinology 153:1341–1351. DOI:https://doi.org/10.1210/en.2011-1663

(54) Yong L, Thet Z, Zhu Y. 2017. Genetic editing of the androgen receptor contributes to impaired male courtship behavior in zebrafish. Journal of Experimental Biology 220:3017–3021.DOI:https://doi.org/10.1242/jeb.161596

There are a surprising number of citations not included; some of the ones not included argue against the authors' claims that their findings were "contrary to expectation"

In our previous revision, we cited the relevant references (Hallgren et al., 2006; O’Connell and Hofmann, 2012; Huffman et al., 2013; Jalabert et al., 2015) in the Introduction. We also revised the text to remove phrases such as “contrary to expectation” and “unexpected.”

The experimental design for studying aggression in males has flaws. A standard test like a residentintruder test should be used.

Following this comment, we have attempted additional aggression assays using the resident-intruder paradigm. However, these experiments did not produce consistent or interpretable results. As noted in our previous revision, medaka naturally form shoals and exhibit weak territoriality, and even slight differences in dominance between a resident and an intruder can markedly increase variability, reducing data reliability. Therefore, we believe that the approach used in the present study provides a more suitable assessment of aggression in medaka, regardless of territorial tendencies. We will continue to explore potential refinements in future studies and respectfully ask the reviewer to evaluate the present work based on the assay used here.

While they investigate males and females, there are fewer experiments and explanations for the female results, making it feel like a small addition or an aside

While we did not adopt this comment in our previous revision, we have carefully reconsidered the reviewers’ feedback and have now decided to remove the female data. This change allows us to present a more focused and cohesive story centered on males. The specific revisions are outlined below:

Abstract

Line 25: The text “, thereby revealing a previously unappreciated mode of action of brain-derived estrogens. We additionally show that female fish lacking Cyp19a1b are less receptive to male courtship and conversely court other females, highlighting the significance of brain-derived estrogens in establishing sex-typical behaviors in both sexes.” has been revised to “. Taken together, these findings reveal a previously unappreciated mode of action of brain-derived estrogens in shaping male-typical behaviors.”

Results

Line 88: The text “Loss of cyp19a1b function in these fish was verified by measuring brain and peripheral levels of sex steroids. As expected, brain estradiol-17β (E2) in both male and female homozygous mutants (cyp19a1b^−/−) was significantly reduced to 16% and 50%, respectively, of the levels in their wild-type (cyp19a1b^+/+) siblings (P = 0.0037, males; P = 0.0092, females) (Fig. 1, A and B). In males, brain E2 in heterozygotes (cyp19a1b^−/−) was also reduced to 45% of the level in wild-type siblings (P = 0.0284) (Fig. 1A), indicating a dosage effect of cyp19a1b mutation. In contrast, peripheral E2 levels were unaltered in both cyp19a1b^−/− males and females (Fig. S1, C and D), consistent with the expected functioning of Cyp19a1b primarily in the brain. Strikingly, brain levels of testosterone, as opposed to E2, increased 2.2-fold in cyp19a1b^−/− males relative to wild-type siblings (P = 0.0006) (Fig. 1A). Similarly, brain 11KT levels in cyp19a1b^−/− males and females increased 6.2- and 1.9-fold, respectively, versus wild-type siblings (P = 0.0007, males; P = 0.0316, females) (Fig. 1, A and B). These results show that cyp19a1b-deficient fish have reduced estrogen levels coupled with increased androgen levels in the brain, confirming the loss of cyp19a1b function. They also suggest that the majority of estrogens in the male brain and half of those in the female brain are synthesized locally in the brain. In addition, peripheral 11KT levels in cyp19a1b^−/− males and females increased 3.7- and 1.8-fold, respectively (P = 0.0789, males; P = 0.0118, females) (Fig. S1, C and D), indicating peripheral influence in addition to central effects.” has been revised to “Loss of cyp19a1b function in these fish was verified by measuring brain and peripheral levels of sex steroids in males. As expected, brain estradiol-17β (E2) in homozygous mutants (cyp19a1b^−/−) was significantly reduced to 16% of the levels in wild-type (cyp19a1b^+/+) siblings (P = 0.0037) (Figure 1A). Brain E2 in heterozygotes (cyp19a1b^+/−) was also reduced to 45% of wild-type levels (P = 0.0284) (Figure 1A), indicating a dosage effect of the cyp19a1b mutation. In contrast, peripheral E2 levels were unaltered in cyp19a1b^−/− males (Figure 1B), consistent with the expected functioning of Cyp19a1b primarily in the brain. Strikingly, brain testosterone levels, as opposed to E2, increased 2.2-fold in cyp19a1b^−/− males relative to wild-type siblings (P = 0.0006) (Figure 1A). Similarly, brain 11KT levels increased 6.2-fold (P = 0.0007) (Figure 1A). These results indicate that cyp19a1b-deficient males have reduced estrogen coupled with elevated androgen levels in the brain, confirming the loss of cyp19a1b function. They also suggest that the majority of estrogens in the male brain are synthesized locally in the brain. Peripheral 11KT levels also increased 3.7-fold in cyp19a1b^−/− males (P = 0.0789) (Figure 1B), indicating peripheral influence in addition to central effects.”

Line 211: “expression of vt in the pNVT of cyp19a1b^−/− males was significantly reduced to 18% as compared with cyp19a1b^+/+ males (P = 0.0040), a level comparable to that observed in females” has been revised to “expression of vt in the pNVT of cyp19a1b^−/− males was significantly reduced to 18% as compared with cyp19a1b^+/+ males (P = 0.0040).”

The subsection entitled “cyp19a1b-deficient females are less receptive to males and instead court other females,” which followed line 311, has been removed.

Discussion

The two paragraphs between lines 373 and 374, which addressed the female data, have been removed.

Materials and methods

Line 433: “males and females” has been changed to “males”.

Line 457: “focal fish” has been changed to “focal male”.

Line 458: “stimulus fish” has been changed to “stimulus female”.

Line 458: “Fig. 6, E and F, ” has been deleted.

Line 460: “; wild-type males in Fig. 6, A to C” has been deleted.

Line 466: The text “The period of interaction/recording was extended to 2 hours in tests of courtship displays received from the stimulus esr2b-deficient female and in tests of mating behavior between females, because they take longer to initiate courtship (12). In tests using an esr2b-deficient female as the stimulus fish, where the latency to spawn could not be calculated because these fish were unreceptive to males and did not spawn, the sexual motivation of the focal fish was instead assessed by counting the number of courtship displays and wrapping attempts in 30 min. The number of these mating acts was also counted in tests to evaluate the receptivity of females. In tests of mating behavior between two females, the stimulus female was marked with a small notch in the caudal fin to distinguish it from the focal female.” has been revised to “In tests using an esr2b-deficient female as the stimulus fish, the latency to spawn could not be calculated because the female was unreceptive to males and did not spawn. Therefore, the sexual motivation of the focal male was assessed by counting the number of courtship displays and wrapping attempts in 30 min. To evaluate courtship displays performed by stimulus esr2bdeficient females toward focal males, the recording period was extended to 2 hours, as these females take longer to initiate courtship (Nishiike et al., 2021). In all video analyses, the researcher was blind to the fish genotype and treatment.”

Line 499: “brains dissected from males and females of the cyp19a1b-deficient line (analysis of ara, arb, vt, gal, npba, and esr2b) and males of the esr1-, esr2a-, and esr2b-deficient lines” has been revised to “male brains from the cyp19a1b-deficient line (analysis of ara, arb, vt, and gal) and from the esr1-, esr2a-, and esr2b-deficient lines.”

Line 504: “After color development for 15 min (gal), 40 min (npba), 2 hours (vt), or overnight (ara, arb, and esr2b)” has been revised to “After color development for 15 min (gal), 2 hours (vt), or overnight (ara and arb).”

Line 516: “Thermo Fisher Scientific, Waltham, MA” has been changed to “Thermo Fisher Scientific” to avoid redundancy.

Line 565: The subsection entitled “Measurement of spatial distances between fish” has been removed.

Line 585: “6/10 cyp19a1b^+/+, 3/10 cyp19a1b^+/−, and 6/10 cyp19a1b^−/− females were excluded in Fig. 6B;” has been deleted.

References

The following references have been removed:

Capel B. 2017. Vertebrate sex determination: evolutionary plasticity of a fundamental switch. Nature Reviews Genetics 18:675–689. DOI: https://doi.org/10.1038/nrg.2017.60

Hiraki T, Nakasone K, Hosono K, Kawabata Y, Nagahama Y, Okubo K. 2014. Neuropeptide B is femalespecifically expressed in the telencephalic and preoptic nuclei of the medaka brain. Endocrinology 155:1021–1032. DOI: https://doi.org/10.1210/en.2013-1806

Juntti SA, Hilliard AT, Kent KR, Kumar A, Nguyen A, Jimenez MA, Loveland JL, Mourrain P, Fernald RD. 2016. A neural basis for control of cichlid female reproductive behavior by prostaglandin F2α. Current Biology 26:943–949. DOI: https://doi.org/10.1016/j.cub.2016.01.067

Kimchi T, Xu J, Dulac C. 2007. A functional circuit underlying male sexual behaviour in the female mouse brain. Nature 448:1009–1014. DOI: https://doi.org/10.1038/nature06089

Kobayashi M, Stacey N. 1993. Prostaglandin-induced female spawning behavior in goldfish (Carassius auratus) appears independent of ovarian influence. Hormones and Behavior 27:38–55.

DOI:https://doi.org/10.1006/hbeh.1993.1004

Liu H, Todd EV, Lokman PM, Lamm MS, Godwin JR, Gemmell NJ. 2017. Sexual plasticity: a fishy tale. Molecular Reproduction and Development 84:171–194. DOI: https://doi.org/10.1002/mrd.22691

Munakata A, Kobayashi M. 2010. Endocrine control of sexual behavior in teleost fish. General and Comparative Endocrinology 165:456–468. DOI: https://doi.org/10.1016/j.ygcen.2009.04.011

Nugent BM, Wright CL, Shetty AC, Hodes GE, Lenz KM, Mahurkar A, Russo SJ, Devine SE, McCarthy MM. 2015. Brain feminization requires active repression of masculinization via DNA methylation. Nature Neuroscience 18:690–697. DOI: https://doi.org/10.1038/nn.3988

Shaw K, Therrien M, Lu C, Liu X, Trudeau VL. 2023. Mutation of brain aromatase disrupts spawning behavior and reproductive health in female zebrafish. Frontiers in Endocrinology 14:1225199.

DOI:https://doi.org/10.3389/fendo.2023.1225199

Stacey NE. 1976. Effects of indomethacin and prostaglandins on the spawning behaviour of female goldfish. Prostaglandins 12:113–126. DOI: https://doi.org/10.1016/s0090-6980(76)80010-x

Figure 1

Panel B, which originally showed steroid levels in female brains, has been replaced with steroid levels in the periphery of males, originally presented in Figure S1, panel C. Accordingly, the legend “(A and B) Levels of E2, testosterone, and 11KT in the brain of adult cyp19a1b^+/+, cyp19a1b^+/−, and cyp19a1b^−/− males (A) and females (B) (n = 3 per genotype and sex).” has been revised to “(A, B) Levels of E2, testosterone, and 11KT in the brain (A) and periphery (B) of adult cyp19a1b^+/+, cyp19a1b^+/−, and cyp19a1b^−/− males (n = 3 per genotype).”

Figure 3

The female data have been deleted from Figure 3. The revised Figure 3 is presented.

The corresponding legend text has been revised as follows:

Line 862: “males and females (n = 4 and 5 per genotype for males and females, respectively)” has been changed to “males (n = 4 per genotype)”.

Line 864: “males and females (n = 4 except for cyp19a1b^+/+ males, where n = 3)” has been changed to “males (n = 3 and 4, respectively)”.

Figure 6

Figure 6 and its legend have been removed.

Figure 1—figure supplement 1

Panel C, showing male data, has been moved to Figure 1B, as described above, while panel D, showing female data, has been deleted. The corresponding legend “(C and D) Levels of E2, testosterone, and 11KT in the periphery of adult cyp19a1b^+/+, cyp19a1b^+/−, and cyp19a1b^−/− males (C) and females (D) (n = 3 per genotype and sex). Statistical differences were assessed by Bonferroni’s post hoc test (C and D). Error bars represent SEM. *P < 0.05.” has also been removed.

Line 804: Following this change, the figure title has been updated from “Generation of cyp19a1bdeficient medaka and evaluation of peripheral sex steroid levels” to “Generation of cyp19a1b-deficient medaka.”

The statistics comparing "experimental to experimental" and "control to experimental" isn't appropriate 

This comment is the same as one raised in the first review (Reviewer #1’s comment 7 on weaknesses), which we already addressed in our initial revision. For the reviewer’s convenience, we provide the response below:

The reviewer raised concerns about the statistical analysis used for Figures 4C and 4E, suggesting that Bonferroni’s test should be used instead of Dunnett’s test. However, Dunnett’s test is commonly used to compare treatment groups to a reference group that receives no treatment, as in our study. Since we do not compare the treated groups with each other, we believe Dunnett’s test is the most appropriate choice.

Line 576: The reviewer’s concern may have arisen from the phrase “comparisons between control and experimental groups” in the Materials and methods. We have revised it to “comparisons between untreated and E2-treated groups in Figure 4C and D” for clarity.

Reviewer #3 (Public Review):

Summary:

Taking advantage of the existence in fish of two genes coding for estrogen synthase, the enzyme aromatase, one mostly expressed in the brain (Cyp19a1b) and the other mostly found in the gonads (Cyp19a1a), this study investigates the role of brain-derived estrogens in the control of sexual and aggressive behavior in medaka. The constitutive deletion of Cyp19a1b markedly reduced brain estrogen content in males and to a lesser extent in females. These effects are accompanied by reduced sexual and aggressive behavior in males and reduced preference for males in females. These effects are reversed by adult treatment with supporting a role for estrogens. The deletion of Cyp19a1b is associated with a reduced expression of the genes coding for the two androgen receptors, ara and arb, in brain regions involved in the regulation of social behavior. The analysis of the gene expression and behavior of mutants of estrogen receptors indicates that these effects are likely mediated by the activation of the esr1 and esr2a isoforms. These results provide valuable insight into the role of estrogens in social behavior in the most abundant vertebrate taxon, however the conclusion of brain-derived estrogens awaits definitive confirmation.

We thank this reviewer for their positive evaluation of our work and comments that have improved the manuscript.

Strength:

Evaluation of the role of brain "specific" Cyp19a1 in male teleost fish, which as a taxon are more abundant and yet proportionally less studied that the most common birds and rodents. Therefore, evaluating the generalizability of results from higher vertebrates is important. This approach also offers great potential to study the role of brain estrogen production in females, an understudied question in all taxa.

Results obtained from multiple mutant lines converge to show that estrogen signaling, likely synthesized in the brain drives aspects of male sexual behavior.

The comparative discussion of the age-dependent abundance of brain aromatase in fish vs mammals and its role in organization vs activation is important beyond the study of the targeted species.  - The authors have made important corrections to tone down some of the conclusions which are more in line with the results. 

We thank the reviewer again for their positive evaluation of our work and the revisions we have made.

weaknesses:

No evaluation of the mRNA and protein products of Cyp19a1b and ESR2a are presented, such that there is no proper demonstration that the mutation indeed leads to aromatase reduction. The conclusion that these effects dependent on brain derived estrogens is therefore only supported by measures of E2 with an EIA kit that is not validated. No discussion of these shortcomings is provided in the discussion thus further weakening the conclusion manuscript.

In response to this and other comments, we have now provided direct validation that the cyp19a1b mutation in our medaka leads to loss of function. Real-time PCR analysis showed that cyp19a1b transcript levels in the brain were reduced by approximately half in cyp19a1b^+/− males and were nearly absent in cyp19a1b^−/− males, consistent with nonsense-mediated mRNA decay

In addition, AlphaFold 3-based structural modeling indicated that the mutant Cyp19a1b protein lacks essential motifs, including the aromatic region and heme-binding loop, and exhibits severe conformational distortion (see figure; key structural features are annotated as follows: membrane helix (blue), aromatic region (red), and heme-binding loop (orange)). 

Results:

Line 101: The following text has been added: “Loss of cyp19a1b function was further confirmed by measuring cyp19a1b transcript levels in the brain and by predicting the three-dimensional structure of the mutant protein. Real-time PCR revealed that transcript levels were reduced by half in cyp19a1b^+/− males and were nearly undetectable in cyp19a1b^−/− males, presumably as a result of nonsense-mediated mRNA decay (Lindeboom et al., 2019) (Figure 1C). The wild-type protein, modeled by AlphaFold 3, exhibited a typical cytochrome P450 fold, including the membrane helix, aromatic region, and hemebinding loop, all arranged in the expected configuration (Figure 1—figure supplement 1C). The mutant protein, in contrast, was severely truncated, retaining only the membrane helix (Figure 1—figure supplement 1C). The absence of essential domains strongly indicates that the allele encodes a nonfunctional Cyp19a1b protein. Together, transcript and structural analyses consistently demonstrate that the mutation generated in this study causes a complete loss of cyp19a1b function.”

Materials and methods

Line 438: A subsection entitled “Real-time PCR” has been added. The text of this subsection is as follows: “Total RNA was isolated from the brains of cyp19a1b^+/+, cyp19a1b^+/−, and cyp19a1b^−/− males using the RNeasy Plus Universal Mini Kit (Qiagen, Hilden, Germany). cDNA was synthesized with the SuperScript VILO cDNA Synthesis Kit (Thermo Fisher Scientific, Waltham, MA). Real-time PCR was performed on the LightCycler 480 System II using the LightCycler 480 SYBR Green I Master (Roche Diagnostics). Melting curve analysis was conducted to verify that a single amplicon was obtained in each sample. The β-actin gene (actb; GenBank accession number NM_001104808) was used to normalize the levels of target transcripts. The primers used for real-time PCR are shown in Supplementary file 2.”

Line 448: A subsection entitled “Protein structure prediction” has been added. The text of this subsection is as follows: “Structural predictions of Cyp19a1b proteins were conducted using AlphaFold 3 (Abramson et al., 2024). Amino acid sequences corresponding to the wild-type allele and the mutant allele generated in this study were submitted to the AlphaFold 3 prediction server. The resulting models were visualized with PyMOL (Schrödinger, New York, NY), and key structural features, including the membrane helix, aromatic region, and heme-binding loop, were annotated.”

References

The following two references have been added:

Abramson J, Adler J, Dunger J, Evans R, Green T, Pritzel A, Ronneberger O, Willmore L, Ballard AJ, Bambrick J, Bodenstein SW, Evans DA, Hung CC, O'Neill M, Reiman D, Tunyasuvunakool K, Wu Z, Žemgulytė A, Arvaniti E, Beattie C, Bertolli O, Bridgland A, Cherepanov A, Congreve M, CowenRivers AI, Cowie A, Figurnov M, Fuchs FB, Gladman H, Jain R, Khan YA, Low CMR, Perlin K, Potapenko A, Savy P, Singh S, Stecula A, Thillaisundaram A, Tong C, Yakneen S, Zhong ED, Zielinski M, Žídek A, Bapst V, Kohli P, Jaderberg M, Hassabis D, Jumper JM. 2024. Accurate structure prediction of biomolecular interactions with AlphaFold 3. Nature 630:493–500. DOI: https://doi.org/10.1038/s41586-024-07487-w

Lindeboom RGH, Vermeulen M, Lehner B, Supek F. 2019. The impact of nonsense-mediated mRNA decay on genetic disease, gene editing and cancer immunotherapy. Nature Genetics 51:1645–1651.DOI:https://doi.org/10.1038/s41588-019-0517-5

Figure 1

The real-time PCR results described above have been incorporated in Figure 1, panel C, with the corresponding legend provided below (line 788).

(C) Brain cyp19a1b transcript levels in cyp19a1b^+/+, cyp19a1b^+/−, and cyp19a1b^−/− males (n = 6 per genotype). Mean value for cyp19a1b^+/+ males was arbitrarily set to 1.

The subsequent panels have been renumbered accordingly. The entirety of the revised Figure 1.

Figure 1—figure supplement 1

The AlphaFold 3-generated structural models described above have been incorporated in Figure 1— figure supplement 1, panel C, with the corresponding legend provided below (line 811).

(C) Predicted three-dimensional structures of wild-type (left) and mutant (right) Cyp19a1b proteins. Key structural features are annotated as follows: membrane helix (blue), aromatic region (red), and heme-binding loop (orange).

The entirety of the revised Figure 1—figure supplement 1 is presented

The information on the primers used for real-time PCR has been included in Supplementary file 2.

The functional deficiency of esr2a was already addressed in the previous revision. For clarity, we have reproduced the relevant information here.

A previous study reported that female medaka lacking esr2a fail to release eggs due to oviduct atresia (Kayo et al., 2019, Sci Rep 9:8868). Similarly, in this study, some esr2a-deficient females exhibited spawning behavior but were unable to release eggs, although the sample size was limited (Δ8 line: 2/3; Δ4 line: 1/1). In contrast, this was not observed in wild-type females (Δ8 line: 0/12; Δ4 line: 0/11). These results support the effective loss of esr2a function. To incorporate this information into the manuscript, the following text has been added to the Materials and methods (line 423): “A previous study reported that esr2a-deficient female medaka cannot release eggs due to oviduct atresia (Kayo et al., 2019). Likewise, some esr2a-deficient females generated in this study, despite the limited sample size, exhibited spawning behavior but were unable to release eggs (Δ8 line: 2/3; Δ4 line: 1/1), while such failure was not observed in wild-type females (Δ8 line: 0/12; Δ4 line: 0/11). These results support the effective loss of esr2a function.”

Most experiments are weakly powered (low sample size).

This comment is essentially the same as one raised in the first review (Reviewer #3’s comment 7 on weaknesses). We acknowledge the reviewer’s concern that the histological analyses were weakly powered due to the limited sample size. In our earlier revision, we responded as follows:

Histological analyses were conducted with a relatively small sample size, as our previous experience suggested that interindividual variability in the results would not be substantial. Since significant differences were detected in many analyses, further increasing the sample size was deemed unnecessary.

The variability of the mRNA content for a same target gene between experiments (genotype comparison vs E2 treatment comparison) raises questions about the reproducibility of the data (apparent disappearance of genotype effect).

This comment is the same as one raised in the first review (Reviewer #3’s comment 8 on weaknesses), which we already addressed in our initial revision. For the reviewer’s convenience, we provide the response below:

As the reviewer pointed out, the overall area of ara expression is larger in Figure 2J than in Figure 2F. However, the relative area ratios of ara expression among brain nuclei are consistent between the two figures, indicating the reproducibility of the results. Thus, this difference is unlikely to affect the conclusions of this study.

Additionally, the differences in ara expression in pPPp and arb expression in aPPp between wild-type and cyp19a1b-deficient males appear less pronounced in Figures 2J and 2K than in Figures 2F and 2H. This is likely attributable to the smaller sample size used in the experiments for Figures 2J and 2K, resulting in less distinct differences. However, as the same genotype-dependent trends are observed in both sets of figures, the conclusion that ara and arb expression is reduced in cyp19a1b-deficient male brains remains valid.

Conclusions:

Overall, the claims regarding role of estrogens originating in the brain on male sexual behavior is supported by converging evidence from multiple mutant lines. The role of brain-derived estrogens on gene expression in the brain is weaker as are the results in females. 

We appreciate the reviewer’s positive evaluation of our findings on male behavior. The concern regarding the role of brain-derived estrogens in gene expression has been addressed in our rebuttal, and the female data have been removed so that the analysis now focuses on males. The specific revisions for removing the female data are described in Response to reviewer #1’s comment 6 on weaknesses.

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors):

The manuscript is improved slightly. I am thankful the authors addressed some concerns, but for several concerns the referees raised, the authors acknowledged them yet did not make corresponding changes to the manuscript or disagreed that they were issues at all without explanation. All reviewers had issues with the imbalanced focus on males versus females and the male aggression assay. Yet, they did not perform additional experiments or even make changes to the framing and scope of the manuscript. If the authors had removed the female data, they may have had a more cohesive story, but then they would still be left with inadequate behavior assays in the males. If the authors don't have the time or resources to perform the additional work, then they should have said so. However, the work would be incomplete relative to the claims. That is a key point here. If they change their scope and claims, the authors avoid overstating their findings. I want to see this work published because I believe it moves the field forward. But the authors need to be realistic in their interpretations of their data. 

In response to this and related comments, we have removed the female data and focused the manuscript on analyses in males. The specific revisions are described in Response to reviewer #1’s comment 6 on weaknesses. Additionally, we have validated that the cyp19a1b mutation in our medaka leads to loss of function (see Response to reviewer #3’s comment 1 on weaknesses), which further strengthens the reliability of our conclusions regarding male behavior.

I agree with the reviewer who said we need to see validation of the absence of functional cyp19a1 b in the brain. However, the results from staining for the protein and performing in situ could be quizzical. Indeed, there aren't antibodies that could distinguish between aromatase a and b, and it is not uncommon for expression of a mutated gene to be normal. One approach they could do is measure aromatase activity, but they are *sort of* doing that by measuring brain E2. It's not perfect, but we teleost folks are limited in these areas. At the very least, they should show the predicted protein structure of the mutated aromatase alleles. It could show clearly that the tertiary structure is utterly absent, giving more support to the fact that their aromatase gene is non-functional. 

As noted above, we have further validated the loss of cyp19a1b function by measuring cyp19a1b transcript levels in the brain and predicting the three-dimensional structure of the mutant protein. These analyses confirmed that cyp19a1b function is indeed lost, thereby increasing the reliability of our conclusions. For further details, please refer to Response to reviewer #3’s comment 1 on weaknesses.

With all of this said, the work is important, and it is possible that with a reframing of the impact of their work in the context of their findings, I could consider the work complete. I think with a proper reframing, the work is still impactful. 

In accordance with this feedback, and as described above, we have reframed the manuscript by removing the female data and focusing exclusively on males. This revision clarifies the scope of our study and reinforces the support for our conclusions. For further details, please refer to Response to reviewer #1’s comment 6 on weaknesses.

(1) Clearly state in the Figure 1 legend that each data point for male aggressive behaviors represents the total # of behaviors calculated over the 4 males in each experimental tank.

In response to this comment, we have revised the legend of Figure 1K (line 797). The original legend, “(K) Total number of each aggressive act observed among cyp19a1b^+/+, cyp19a1b^+/−, or cyp19a1^−/− males in the tank (n = 6, 7, and 5, respectively),” has been updated to “(K) Total number of each aggressive act performed by cyp19a1b^+/+, cyp19a1b^+/−, and cyp19a1b^−/− males. Each data point represents the sum of acts recorded for the 4 males of the same genotype in a single tank (n = 6, 7, and 5 tanks, respectively).” This clarifies that each data point reflects the total behaviors of the 4 males within each tank.

(2) The authors wrote under "Response to reviewer #1's major comment "...the development of male behaviors may require moderate neuroestrogen levels that are sufficient to induce the expression of ara and arb, but not esr2b, in the underlying neural circuitry": "This may account for the lack of aggression recovery in E2-treated cyp19a1b-deficient males in this study.".

What is meant by the latter statement? What accounts for the lack of aggression? The lack of increase in esr2b? Please clarify. 

Line 365: In response to this comment, “This may account for the lack of aggression recovery in E2treated cyp19a1b-deficient males in this study.” has been revised to “Considering this, the lack of aggression recovery in E2-treated cyp19a1b-deficient males in this study may be explained by the possibility that the E2 dose used was sufficient to induce not only ara and arb but also esr2b expression in aggression-relevant circuits, which potentially suppressed aggression.”

This revision clarifies that, while moderate brain estrogen levels are sufficient to promote male behaviors via induction of ara and arb, the E2 dose used in this study may have additionally induced esr2b in circuits relevant to aggression, potentially underlying the lack of aggression recovery.

(3) This is a continuation of my comment/concern directly above. If the induction of ara and arb aren't enough, then how can, as the authors state, androgen signaling be the primary driver of these behaviors? 

In response to this follow-up comment, we would like to clarify that, as described above, the lack of aggression recovery in E2-treated cyp19a1b-deficient males is not due to insufficient induction of ara and arb, but instead is likely because esr2b was also induced in aggression-relevant circuits, which may have suppressed aggression. Therefore, the concern that androgen signaling cannot be the primary driver of these behaviors is not applicable.

(4) The authors' point about sticking with the terminology for the ar genes as "ara" and "arb" is not convincing. The whole point of needing a change to match the field of neuroendocrinology as a whole (that is, across all vertebrates) is researchers, especially those with high standing like the Okubo group, adopt the new terminology. Indeed, the Okubo group is THE leader in medaka neuroendocrinology. It would go a long way if they began adopting the new terminology of "ar1" and "ar2". I understand this may be laborious to a degree, and each group can choose to use their terminology, but I'd be remiss if I didn't express my opinion that changing the terminology could help our field as a whole. 

We sincerely appreciate the reviewer’s thoughtful comments regarding nomenclature consistency in vertebrate neuroendocrinology. We understand the motivation behind the suggestion to adopt ar1 and ar2. However, we consider the established nomenclature of ara and arb to be more appropriate for the following reasons.

First, adopting the ar1/ar2 nomenclature would introduce a discrepancy between gene and protein symbols. According to the NCBI International Protein Nomenclature Guidelines (Section 2B.Abbreviations and symbols;

https://www.ncbi.nlm.nih.gov/genbank/internatprot_nomenguide/), the ZFIN Zebrafish Nomenclature Conventions (Section 2. PROTEINS:https://zfin.atlassian.net/wiki/spaces/general/pages/1818394635/ZFIN+Zebrafish+Nomenclature+Con ventions), and the author guidelines of many journal

(e.g.,https://academic.oup.com/molehr/pages/Gene_And_Protein_Nomenclature), gene and protein symbols should be identical (with proteins designated in non-italic font and with the first letter capitalized). Maintaining consistency between gene and protein symbols helps avoid unnecessary confusion. The ara/arb nomenclature allows this, whereas ar1/ar2 does not.

Second, the two androgen receptor genes in teleosts are paralogs derived from the third round of wholegenome duplication that occurred early in teleost evolution. For such duplicated genes, the ZFIN Zebrafish Nomenclature Conventions (Section 1.2. Duplicated genes) recommend appending the suffixes “a” and “b” to the approved symbol of the human or mouse ortholog. This convention clearly indicates that these genes are whole-genome duplication paralogs and provides an intuitive way to represent orthologous and paralogous relationships between teleost genes and those of other vertebrates. As a result, it has been widely adopted, and we consider it logical and beneficial to apply the same principle to androgen receptors.

In light of these considerations, we respectfully maintain that the ara/arb nomenclature is more suitable for the present manuscript than the alternative ar1/ar2 system.

(5) In the discussion please discuss these potentially unexpected findings.

(a) gal was unaffected in female cyp19a1 mutants, but they exhibit mating behaviors towards females. Given gal is higher in males and these females act like females, what does this mean about the function of gal/its utility in being a male-specific marker (is it one??)? 

(b) esr2b expression is higher in female cyp19a1 mutants. this is unexpected as well given esr2b is required for female-typical mating and is higher in females compared to males and E2 increases esr2b expression. please explain...well, what this means for our idea of what esr2b expression tell us. 

We thank the reviewer for the insightful comments. As the female data have been removed from the manuscript, discussion of these findings in female cyp19a1b mutants is no longer necessary.

Reviewer #3 (Recommendations For The Authors):

The authors have addressed a number of answers to the reviewer's comments, notably they provided missing methodological information and rephrased the text. However, the authors have not addressed the main issues raised by the reviewers. Notably, it is regrettable that the reduced amount of brain aromatase cannot be confirmed, this seems to be the primary step when validating a new mutant. Even if protein products of the two genes may not be discriminated (which I can understand), it should be possible to evaluate the expression of a common messenger and/or peptide and confirm that aromatase expression is reduced in the brain. Since Cyp19a1b is relatively more abundant in the brain Cyp19a1a, this would strengthen the conclusion and provide confidence that the mutant indeed does silence aromatase expression in the brain. Although these short comings are acknowledged in the rebuttal letter, this is not mentioned in the discussion. Doing so would make the manuscript more transparent and clearer. 

As noted in Response to reviewer #3’s comment 1 on weaknesses, we have validated the loss of Cyp19a1b function by measuring its transcript levels in the brain and predicting the three-dimensional structure of the mutant protein. These analyses confirmed that Cyp19a1b function is indeed lost, thereby increasing the reliability of our conclusions.

FigS1 - panels C&D please indicate in which tissue were hormones measured. Blood?

We thank the reviewer for pointing this out. In our study, “peripheral” refers to the caudal half of the body excluding the head and visceral organs, not blood. Accordingly, we have revised the figure legend and the description in the Materials and Methods section as follows:

Legend for Figure 1B (line 787) now reads: “Levels of E2, testosterone, and 11KT in the brain (A) and peripheral tissues (caudal half of the body) (B) of adult cyp19a1b^+/+, cyp19a1b^+/−, and cyp19a1b^−/− males (n = 3 per genotype).”

Materials and methods (line 431): The sentence “Total lipids were extracted from the brain and peripheral tissues (from the caudal half) of” has been revised to “Total lipids were extracted from the brain and from peripheral tissues, specifically the caudal half of the body excluding the head and visceral organs, of.”

Additional Alterations:

We have reformatted the text and supporting materials to comply with the journal’s Author Guidelines. The following changes have been made:

(1) Figures and supplementary files are now provided separately from the main text.

(2) The title page has been reformatted without any changes to its content.

(3) In-text citations have been changed from numerical references to the author–year format.

(4) Figure labels have been revised from “Fig. 1,” “Fig. S1,” etc., to “Figure 1,” “Figure 1—figure supplement 1,” etc.

(5) Table labels have been revised from “Table S1,” etc., to “Supplementary file 1,” etc.

(6) Line 324: The typo “is” has been corrected to “are”.

(7) Line 382: The section heading “Materials and Methods” has been changed to “Materials and methods” (lowercase “m”).

(8) Line 383: The Key Resources Table has been placed at the beginning of the Materials and methods section.

(9) Line 389: The sentence “Sexually mature adults (2–6 months) were used for experiments, and tissues were consistently sampled 1–5 hours after lights on.” has been revised to “Sexually mature adults (2–6 months) were used for experiments and assigned randomly to experimental groups. Tissues were consistently sampled 1–5 hours after lights on.”

(10)  Line 393: The sentence “All fish were handled in accordance with the guidelines of the Institutional Animal Care and Use Committee of the University of Tokyo.” has been removed.

(11)  Line 589: The following sentence has been added: “No power analysis was conducted due to the lack of relevant data; sample size was estimated based on previous studies reporting inter-individual variation in behavior and neural gene expression in medaka.”

(12)  Line 598: The reference list has been reordered from numerical sequence to alphabetical order by author.

(13)  In the figure legends, notations such as “A and B” have been revised to “A, B.”

Author response:

We would like to thank both reviewers for taking the time to review the manuscript in detail. Your comments have been extremely useful and constructive. A revised version of the manuscript will seek to address the weaknesses raised, clarifying the reasons for the assumptions made, the impact they have and how they influence the policy implication of the work. We will clarify the language to differentiate the work from the standard sub-national tailoring which is typically conducted to support National Malaria Programmes and emphasise why our mechanistic model can provide greater information than simple summary statistics.

Author response:

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

Public Reviews:

Reviewer #1 (Public Reviews):

Summary:

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

Strengths:

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

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

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Reviewer #2 (Public Reviews):

Summary:

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

Strengths:

(1)  Careful physiological and imaging studies.

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

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

(4)  Clear analytical techniques.

We thank the reviewer for their appreciation of the study.

Weaknesses:

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

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

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

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

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

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

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

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

Author response image 1.

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

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

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

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

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

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

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

Reviewer #3 (Public Reviews):

Summary:

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

Strengths:

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

We thank the reviewer for finding the study intellectually stimulating.

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

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

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

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

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

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

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

We expanded the discussion accordingly.

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

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

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

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

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

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

We thank the reviewer for suggesting this analysis.

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

Targeting the specific principal whisker is performed under the stereoscope.  

Specifically, we have added this statement in line 628:

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

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

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

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

These are the numbers the reviewer is inquiring about. 

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

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

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

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

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

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

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

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

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

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

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

This is now fixed. (dF/F).

(9) Figure 4: Axis labels are missing.

Added.

Minor: 

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

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

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

We have changed it.

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

The statistics is now presented in current Figure 1E.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Thank you, it is now fixed.

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

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

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

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

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

Thanks, we have now updated the terms.

Reviewer #2 (Recommendations for the authors): 

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

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

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

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

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

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

We have now updated the methods section in line 611: 

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

Reviewer #3 (Recommendations for the authors): 

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

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

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

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

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

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

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

Minor Comments:

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

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

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

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

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

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

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

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

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

We have now clarified this. 

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

Thank you, we have now done it.

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

Thank you, we have now done it.

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

We have changed the structure of this figure.

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

The following paragraph has been added in the methods section:

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

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

We have added them.

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

Each line represents an average response of a neuron.  

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

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

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

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

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

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

References

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

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

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

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

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

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

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

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Author response:

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

eLife Assessment

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

Public Reviews:

Reviewer #1 (Public review):

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

Major strengths of this manuscript include:

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

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

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

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

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

We thank the reviewer for the positive comments.

Reviewer #2 (Public review):

Summary:

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

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

Strengths:

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

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

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

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

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

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

Weaknesses:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

We have revised the Discussion.

Reviewer #3 (Public review):

Summary:

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

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

Thank you for the encouraging remarks.

Strengths:

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

Weaknesses:

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

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

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

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

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

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

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

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

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

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

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

Reviewer #2 (Recommendations for the authors):

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

Good suggestion; we have edited the text accordingly.

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

Point taken…

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

Text edited to indicate that most are efficiently spliced.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

Done.

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

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