Author response:

The following is the authors’ response to the previous reviews

eLife Assessment

This important study introduces an advance in multi-animal tracking by reframing identity assignment as a self-supervised contrastive representation learning problem. It eliminates the need for segments of video where all animals are simultaneously visible and individually identifiable, and significantly improves tracking speed, accuracy, and robustness with respect to occlusion. This innovation has implications beyond animal tracking, potentially connecting with advances in behavioral analysis and computer vision. The strength of support for these advances is compelling overall, although there were some remaining minor methodological concerns.

To tackle “minor methodological concerns” mentioned in the Editorial assessment and Reviewer 3, the new version of the manuscript includes the following changes:

a) The new ms does not anymore use the word “accuracy” but “IDF1 scores”. See, for example, Lines 46, 161, 176, and 522 for our new wording as “IDF1 scores”.

b) Instead of comparing softwares using mean accuracy over the benchmark, Reviewer 3 proposes to use medians or even boxplots. We now provide boxplot results with mean, median, percentiles and outliers (Figure 1- figure Supplement 2).

Additionally, we also include in the text the other recommendations from Reviewer 3:

a) We now more explicitly describe the problems of the original idtracker.ai v4 in the benchmark (lines 66-68). Around half of the videos had a high accuracy in the original dtracker.ai (v4) but the other half of the videos had lower accuracies (Figure 1a, blue). The new idtracker.ai has high accuracy values for all the videos (Figure 1a, magenta).

Also, the videos with high accuracy in the old idtracker.ai had very long tracking times (Figure 1b, blue) and the new version does not (Figure 1b, magenta). So the benchmark allows us to distinguish the new idtracker.ai as having a better accuracy for all videos and lower tracking times, making it a much more practical system than previous ones. 

b) We further clarified the occlusion experiment (lines 188-190 and 277-290).

c) We explain why we measure accuracies with and without animal crossings (lines 49-62).

d) We added a Discussion section (lines 223-244).

We believe the new version has clarified the minor methodological concerns.

Reviewer #3 (Public review):

The authors have reorganized and rewritten a substantial portion of their manuscript, which has improved the overall clarity and structure to some extent. In particular, omitting the different protocols enhanced readability. However, all technical details are now in appendix which is now referred to more frequently in the manuscript, which was already the case in the initial submission. These frequent references to the appendix - and even to appendices from previous versions - make it difficult to read and fully understand the method and the evaluations in detail. A more self-contained description of the method within the main text would be highly appreciated.

In the new ms, we have reduced the references to the appendix by having a more detailed explanation in one place, lines 49-62.

Furthermore, the authors state that they changed their evaluation metric from accuracy to IDF1. However, throughout the manuscript they continue to refer to "accuracy" when evaluating and comparing results. It is unclear which accuracy metric was used or whether the authors are confusing the two metrics. This point needs clarification, as IDF1 is not an "accuracy" measure but rather an F1-score over identity assignments.

We thank the reviewer for noticing this. Following this recommendation, we changed how we refer to the accuracy measure with “IDF1 score” in the entire ms. See, for example, lines 46, 161, 176, and 522.

The authors compare the speedups of the new version with those of the previous ones by taking the average. However, it appears that there are striking outliers in the tracking performance data (see Supplementary Table 1-4). Therefore, using the average may not be the most appropriate way to compare. The authors should consider using the median or providing more detailed statistics (e.g., boxplots) to better illustrate the distributions.

We thank the reviewer for asking for more detailed statistics. We added the requested box plot in Figure 1- figure Supplement 2 to provide more complete statistics in the comparison.

The authors did not provide any conclusion or discussion section. Including a concise conclusion that summarizes the main findings and their implications would help to convey the message of the manuscript.

We added a Discussion section in lines 223-244.

The authors report an improvement in the mean accuracy across all benchmarks from 99.49% to 99.82% (with crossings). While this represents a slight improvement, the datasets used for benchmarking seem relatively simple and already largely "solved". Therefore, the impact of this work on the field may be limited. It would be more informative to evaluate the method on more challenging datasets that include frequent occlusions, crossings, or animals with similar appearances.

Around half of the videos also had a very high accuracy in the original dtracker.ai (v4) but the other half of the videos had lower accuracies (Figure 1a, blue). For example, we found IDF1 scores of 94.47% for a video of 100 zebrafish with thousands of crossings (z_100_1), 93.77% for a video of 4 mice (m_4_2) and 69.66% for a video of 100 flies (d_100_3). The new idtracker.ai has high accuracy values for all the videos (Figure 1a, magenta).

Importantly, the tracking times for the majority of videos was very high in the original idtracker.ai (Figure 1b, blue), making the use of the tracking system limited in practice. The new system manages both a high accuracy in all videos (Figure 1a, magenta) and much lower tracking times (Figure 1b, magenta), making it a much more practical system..

We have added a sentence of the limitations of the original idtracker.ai as obtained from the benchmark, lines 66-68.

The accuracy reported in the main text is "without crossings" - this seems like incomplete evaluation, especially that tracking objects that do not cross seems a straightforward task. Information is missing why crossings are a problem and are dealt with separately.

We have now added an explanation on why we measure accuracy without crossings and why we separated it from the accuracy for all the trajectory in lines 49-62. The reason is that the identification algorithm being presented in this ms only identifies animal images outside the crossings. This algorithm makes robust animal identifications through the video despite the thousands of animal crossings typically existing in each of our videos used in the benchmark. It is a second algorithm (that hasn’t changed since the first idTracker in 2014) the one that assigns animal positions during crossings once the first algorithm has made animal identifications before and after the crossings.

There are several videos with a much lower tracking accuracy, explaining what the challenges of these videos are and why the method fails in such cases would help to understand the method's usability and weak points.

Some videos had low accuracy on previous versions (Figure 1a, blue), but the new idtracker.ai has high accuracy in all of them (Figure 1a, magenta).

Reviewer #3 (Recommendations for the authors):

(1) As described before, the authors claim to use IDF1 as their metric in the whole manuscript (lines 414-436) but only refer to accuracy when presenting the results. It is not clear, whether accuracy was used as a metric instead of IDF1 or the authors are confusing these metrics.

Following this recommendation, we replaced “accuracy” with “IDF1 score” , see lines 46, 161, 176, and 522.

(2) In the introduction, a brief explanation why crossings need to be dealt with separately would help to understand the logic of the method design.

We added such an explanation in lines 49-62.

(3) Figure 3: We asked about how the tracking accuracy is being assessed with occlusions. The authors responded with that only the GT points inside the ROI are taken into account when computing the accuracy. Does this mean, that the occluded blobs are still part of the CNN training and the clustering? This questions the purpose of this experiment, since the accuracy performance would therefore only change, if the errors, that their approach is doing either way, are outside the ROI and, therefore, not part of the metric evaluation.

The occluded blobs are not part of any training because they are erased from the video, they do not exist. We made this more clear in lines 188-190 and 277-290.

(4) Figure 1: The fact that datasets are connected with a line is misleading - there is no connection between the data along the x-axis. A line plot is not an appropriate way to present these results.

The new ms clarifies that the lines are for ease of visualization, see last line in the caption of Figure 1.

(5) Lines 38-39: It is not clear how the CNN can be pretrained for the entire video if there are no global segments or only short ones. Here, the distinction between "no segments", "only short segments" and "pretraining on the entire video" is not explained.

This pretraining protocol is not used in the version of the software we present, so details of this are not as relevant.

(6) Figure 2a: The authors are showing "individual fragments" and individual fragments in a global fragment." However, it seems there are a few blue borders missing. In the text (l. 73-79), they note, that they are displaying them as "examples" but the absence of correct blue borders is confusing.

In the new ms, we have replaced the label “Individual fragments in a global fragment” with “Individual fragments in an example global fragment” in the legend of Figure 2.

(7) Lines 61-63, 148-151, and 162-164: Could the authors clarify why they used the average instead of median when comparing the speedups of the new version and the old ones?

We thank the reviewer for asking for more detailed statistics. We added the requested box plot in Figure 1- figure Supplement 2 to provide more complete statistics in the comparison of accuracies and tracking times for old and new systems.

(8) Lines 140-144: The post-processing steps are not clear. The authors should rather state clearly which processes of the old versions they are using. Then the authors could shortly explain them.

We removed this paragraph and explained in more detail in lines 49-62 which parts of the software are new and which ones are not.

(9) Lines 239-251: Here, the authors are clarifying on a section 1-2 pages before. This information should be directly in that section instead.

Following this recommendation, we clarified the occlusion experiment in the main text (lines 188-191) to make it more self-contained. Still, the flow of the main text is better with some details in Methods.

(10) Line 38: It is not clear how the CNN can be pretrained for the entire video if there are no global segments or only short ones. Here, the distinction between "no segments"

"only short segments" and "pretraining on the entire video" is a bit misleading/underexplained.

See number 5.

(11) Figure 2a: The authors are showing "individual fragments" and individual fragments in a global fragment." However, it seems there are a few blue borders missing. In the text (l. 73-79), they note, that they are displaying them as "examples" but the absence of correct blue borders is confusing.

See number 6.

(12) Figure 2c and line 115-118: "Batches" itself is not meaningful without any information of the batch size. The authors should rather depict the batch size and then the number of epochs. The Figure 2 contains the info 400 positive and 400 negative pairs of images per batch. However, there is no information about the total number of images.

Furthermore, these metrics are inappropriate here, since training is carried out from scratch (or already pre-trained) for every new video, each video has different number of animals, different number of images.

Following this recommendation, we clarified the number of images in each batch (Figure 1c caption and lines 134-138), why we do not work with epochs (lines 700-702), and the idea that the clusters in Figure 2 represent an example and the number of batches needed for the clusters to form depends on the video details.

Appendix 1-figure 1: why do the methods fail? It looks that for certain videos the method is fairly unreliable. What is the reason for the methods to crash and how to avoid this?

Those failures are only for the old idtracker.ai and Trex, not for the method presented here. Our new contrastive algorithm does not fail in any of the videos in the benchmark.

We thank the reviewer for the detailed suggestions. We believe we have incorporated all of them in the new version of the ms.

Reviewer #2 (Public review):

The authors aimed to investigate whether gamma synchrony serves a functional role in figure-ground perception. They specifically sought to test whether the stimulus-dependence of gamma synchrony, often considered a limitation, actually facilitates perceptual grouping. Using the theory of weakly coupled oscillators (TWCO), they developed a framework wherein synchronization depends on both frequency detuning (related to contrast heterogeneity) and coupling strength (related to proximity between visual elements). Through psychophysical experiments with texture discrimination tasks and computational modeling, they tested whether human performance follows patterns predicted by TWCO and whether perceptual learning enhances synchrony-based grouping.

Strengths:

(1) The theoretical framework connecting TWCO to visual perception is innovative and well-articulated, providing a potential mechanistic explanation for how gamma synchrony might contribute to both feature binding and separation.

(2) The methodology combines psychophysical measurements with computational modeling, with a solid quantitative agreement between model predictions and human performance.

(3) In particular, the demonstration that coupling strengths can be modified through experience is remarkable and suggests gamma synchrony could be an adaptable mechanism that improves with visual learning.

(4) The cross-validation approach, wherein model parameters derived from macaque neurophysiology successfully predict human performance, strengthens the biological plausibility of the framework.

Likely Impact and Utility:

This work offers a fresh perspective on the functional role of gamma oscillations in visual perception. The integration of TWCO with perceptual learning provides a novel theoretical framework that could influence future research on neural synchrony.

The computational model, with parameters derived from neurophysiological data, offers a useful tool for predicting perceptual performance based on synchronization principles. This approach might be extended to study other perceptual phenomena and could inspire designs for artificial vision systems.

The learning component of the study may have a particular impact, as it suggests a mechanism by which perceptual expertise develops through modified coupling between neural assemblies. This could influence thinking about perceptual learning more broadly, but also raises questions about the underlying mechanism.

Additional Context:

Historically, the functional significance of gamma oscillations has been debated, with early theories of temporal binding giving way to skepticism based on gamma's stimulus-dependence. This study reframes this debate by suggesting that stimulus-dependence is exactly what makes gamma useful for perceptual grouping.

The successful combination of computational neuroscience and psychophysics is a significant strength of this study.

The field would benefit from future work extending (if possible) these findings to more naturalistic stimuli and directly measuring neural activity during perceptual tasks. Additionally, studies comparing predictions from synchrony-based models against alternative mechanisms would help establish the specificity of the proposed framework.

Comments on revised version:

The authors now soften their claim. However, the paper demonstrates that TWCO-derived predictions quantitatively match human figure-ground perception in texture stimuli, and that a synchrony-based readout provides a viable mapping from stimulus to behavior. Given that they cite (and do not show in this paper) the link to synchrony, what they actually establish is that this particular transformation of stimulus features maps better onto behavior. That's meaningful, but it is not a demonstration of mechanism.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper by Karimian et al proposes an oscillator model tuned to implement binding by synchrony (BBS*) principles in a visual task. The authors set out to show how well these BBS principles explain human behavior in figure-ground segregation tasks. The model is inspired by electrophysiological findings in non-human primates, suggesting that gamma oscillations in early visual cortex implement feature-binding through a synchronization of feature-selective neurons. The psychophysics experiment involves the identification of a figure consisting of gabor annuli, presented on a background of gabor annuli. The participants' task is to identify the orientation of the figure. The task difficulty is varied based on the contrast and density of the gabor annuli that make up the figure. The same figures (without the background) are used as inputs to the oscillator model. The authors report that both the discrimination accuracy in the psychophysics experiment and the synchrony of the oscillators in the proposed model follow a similar "Arnold Tongue" relationship when depicted as a function of the texture-defining features of the figure. This finding is interpreted as evidence for BBS/gamma synchrony being the underlying mechanism of the figure-ground segregation.

Note that I chose to use "BBS" over gamma synchrony (used by the authors) in this review, as I am not convinced that the authors show evidence for synchronization in the gamma-band.

We thank the reviewer for their careful assessment of our manuscript and useful comments that we believe have served to strengthen our work.

Strengths:

The design of the proposed model is well-informed by electrophysiological findings, and the idea of using computational modeling to bridge between intracranial recordings in non-human primates and behavioral results in human participants is interesting. Previous work has criticized the BBS synchrony theory based on the observation that synchronization in the gamma-band is highly localized and the frequency of the oscillation depends on the visual features of the stimulus. I appreciate how the authors demonstrate that frequency-dependence and local synchronization can be features of BBS, and not contradictory to the theory. As such, I feel that this work has the potential to contribute meaningfully to the debate on whether BBS is a biophysically realistic model of feature-binding in visual cortex.

Weaknesses:

I have several concerns regarding the presented claims, assessment of meaning and size of the presented effects, particularly with regard to the absence of a priori defined effect sizes.

Firstly, the paper makes strong claims about the frequency-specificity (i.e., gamma synchrony) and anatomical correlates (early visual cortex) of the observed effects. These claims are informed by previous electrophysiological work in non-human primates but are not directly supported by the paper itself. For instance, the title contains the word "gamma synchrony", but the authors do not demonstrate any EEG/MEG or intracranial data in from their human subjects supporting such claims, nor do they demonstrate that the frequencies in the oscillator model are within the gamma band. I think that the paper should more clearly distinguish between statements that are directly supported by the paper (such as: "an oscillator model based on BBS principles accounts for variance in human behavior") and abstract inferences based on the literature (such as "these effects could be attributed to gamma oscillations in early visual cortex, as the model was designed based on those principles").

We thank the reviewer for this helpful comment and agree that the scope of our claims should be clearly delineated between what is directly supported by our data and what is theoretically inferred from prior literature.

We revised the Abstract, Introduction, and early Discussion to moderate the strength of our statements and make the distinction explicit. The revised title now emphasizes that our study tests principles derived from prior work on gamma synchrony rather than directly demonstrating gamma activity in humans. Throughout the text, we use more cautious phrasing that highlights potential mechanisms and theoretical predictions. The intention of our study was not to position synchrony as the only viable mechanism of figure–ground perception. Rather, our goal was to reinvigorate it as a potential contender by showing that features often cited as limitations of synchrony-based binding may in fact be essential properties of the mechanism. We updated phrasing throughout the manuscript to make this clearer and avoid overstating the study’s contribution.

Importantly, our model is not agnostic with respect to frequency band. Oscillator frequencies exhibited by model units are within the gamma range by design. Frequency emerges directly from the contrast within each oscillator’s receptive field, following an empirically established relationship between stimulus contrast and gamma frequency. To our knowledge, such a robust, quantitative relationship between stimulus features to exact oscillation frequency has not been consistently demonstrated for other frequency bands. This relationship yields gamma-band frequencies for all contrasts used in our simulations. The model is thus indeed a gamma oscillator model of V1, not a generic instantiation of Binding by Synchrony (BBS) principles.

That said, we fully agree with the reviewer that our study cannot demonstrate a direct link between gamma synchrony in visual cortex and human behavior. Our behavioral and modeling results instead show that synchronization principles derived from gamma-band physiology in V1 can predict perceptual performance patterns. We now make this distinction explicit throughout the revised manuscript.

Secondly, unlike the human participants, the model strictly does not perform figure-ground segregation, as it only receives the figure as an input.

We thank the reviewer for the opportunity to clarify our modeling approach. We chose not to model the background to reduce computational cost, since including it requires a substantially larger number of oscillators without changing the model’s predictions. The model thus indeed only receives the figure region as input. We aimed to test the local grouping mechanism predicted by TWCO, rather than to simulate a full figure–ground segregation process including a read-out stage. Our model therefore isolates the conditions under which local synchrony emerges within the figure region, assuming that a downstream read-out mechanism (not explicitly modeled here) would detect regions of coherent activity. The exact nature of such a read-out mechanism was beyond the scope of our work.

To confirm that our simplified model is a valid proxy, we ran additional simulations including the background and found that a coherent figure assembly reliably emerges, as can be seen in the phase-locking patterns relative to a reference oscillator at the center of the figure. This validates that the principles of local grouping we studied in isolation hold even when the figure is embedded in a noisy surround. We have added an explicit note in the Results (paragraph 2) that we only simulate the figure and added Supplementary Figure S1 showing the additional simulations.

Finally, it is unclear what effect sizes the authors would have expected a priori, making it difficult to assess whether their oscillator model represents the data well or poorly. I consider this a major concern, as the relationship between the synchrony of the oscillatory model and the performance of the human participants is confounded by the visual features of the figure. Specifically, the authors use the BBS literature to motivate the hypothesis that perception of the texture-defined figure is related to the density and contrast heterogeneity of the texture elements (gabor annuli) of the figure. This hypothesis has to be true regardless of synchrony, as the figure will be easier to spot if it consists of a higher number of high-contrast gabors than the background. As the frequency and phase of the oscillators and coupling strength between oscillators in the grid change as a function of these visual features, I wonder how much of the correlation between model synchrony and human performance is mediated by the features of the figure. To interpret to what extent the similarity between model and human behavior relies on the oscillatory nature of the model, the authors should find a way to estimate an empirical threshold that accounts for these confounding effects. Alternatively, it would be interesting to understand whether a model based on competing theories (e.g., Binding by Enhanced Firing, Roelfsema, 2023) would perform better or worse at explaining the data.

We thank the reviewer for these insightful and constructive comments, which have prompted additional analyses that we believe substantially strengthen our work. The reviewer raises two main points: (1) the need for a benchmark to assess our model’s performance, and (2) the concern that the relationship between model synchrony and behavior might be a non-causal “confound” of the visual features. We address each point below.

(1) Benchmarking model performance

We agree that it is important to assess how well our model performs relative to the data and included this in the original manuscript. We did not predefine an absolute good fit threshold because absolute agreement depends on irreducible noise and inter-subject variability, making a universal cutoff arbitrary. Instead, we had benchmarked model performance in two complementary ways. First, the noise ceiling shown in Figure 5 provides an empirical benchmark for the maximum fit any model could achieve on our data. Simulated Arnold tongues (based on synchrony) approach this ceiling achieving 89% of possible similarity for correlation and 79% of possible similarity for weighted Jaccard similarity, respectively. Second, the parameter sweep (Figure 3) situates our model’s performance within the broader parameter space. It shows that the model, whose key parameters were fixed a priori from independent macaque neurophysiological data, lies close to the optimal regime for explaining the human data. It also provides an estimate of the lower bound (worst-performing point) on the fit that a misspecified model implementing the identical mechanism would achieve. Our model with fixed a priori parameters does 1.41 times better than a misspecified model for the correlation fit metric and 3 times better for weighted Jaccard similarity.

(2) Synchrony as mechanism vs. potential confound

We appreciate the reviewer’s suggestion to test whether synchrony explains behavior beyond stimulus features. In our framework, synchrony is a near-deterministic function of the manipulated stimulus features given fixed model parameters. As a result, synchrony and the stimulus features are collinear (R²≈0.8) leaving no independent variance for synchrony to explain once stimulus features are included. Adding both into one statistical model yields unstable coefficients and no out-of-sample improvement.

Mechanistically, we believe the relevant question is not whether synchrony explains behavior beyond stimulus features but whether synchrony is the correct transformation of the stimulus features to reproduce the behavioral pattern. Please note that in our design we ensured that mean contrast and luminance are identical in the figure and the background such that there are not more high-contrast Gabors in the figure than in the background. We did this with the aim to render mean contrast not a relevant feature. However, there are more high-contrast Gabors in the background, and it is conceivable that the absence of such high contrasts in the figure drives the detection/discrimination of the figure. We therefore agree that testing alternative models would further clarify the unique explanatory value of the synchrony mechanism. To that end, we derived two alternative rate-based readouts from the same V1 simulations of our model from which we derived synchrony. First, average firing rates inside the figure and second, the difference between average firing rates inside the figure and average firing rates in the background (rate difference). We analyzed each individually as predictors of behavior and performed a model comparison based on out-of-sample predictions. While rate difference (but not average firing) showed meaningful associations with performance when considered alone, the synchrony readout had a larger effect size and was favored by the model comparison. We added a new subsection comparing synchrony to rate-based alternatives in the Results (paragraphs 7-9), including additional Bayesian analyses and LOO-CV model comparison. Please note that the model comparison we added to the manuscript provides an additional benchmark beyond the map-level ceiling analysis. It indicates that the mapping from stimulus features to behavior via synchrony generalizes best without requiring an a priori good-fit threshold.

We agree that formally comparing our model to a sophisticated rate-based alternative, such as an instantiation of the Binding by Enhanced Firing model, is an important direction for future work. However, it remains an open and non-trivial question whether such a model could quantitatively reproduce the precise shape of the behavioral Arnold tongue that emerges from the systematic manipulation of our stimulus parameters. Implementing and parameterizing such a model in a comparable, biologically grounded framework is a substantial undertaking that lies beyond the scope of the current study. Therefore, our goal here was not to claim exclusivity for synchrony-based mechanisms, but rather to re-evaluate their plausibility by showing that features often seen as limitations (stimulus dependence and frequency heterogeneity) are, in fact, essential characteristics of the TWCO framework that can predict complex behavioral outcomes.

We would also like to clarify that our stimulus features were derived from theory rather than psychophysical literature. Starting from the principles of TWCO, we mapped frequency detuning and coupling strength onto known anatomical and physiological properties of early visual cortex, and only then derived the corresponding stimulus manipulations (contrast heterogeneity and grid coarseness). Demonstrating that these features predict behavior is therefore not trivial but constitutes a first empirical confirmation that the core TWCO variables match perception.

Apart from adding analyses of additional rate-based readouts of our model, we also refined our discussion of the relationship between these and a synchrony-based mechanism.

Reviewer #2 (Public review):

The authors aimed to investigate whether gamma synchrony serves a functional role in figure-ground perception. They specifically sought to test whether the stimulus-dependence of gamma synchrony, often considered a limitation, actually facilitates perceptual grouping. Using the theory of weakly coupled oscillators (TWCO), they developed a framework wherein synchronization depends on both frequency detuning (related to contrast heterogeneity) and coupling strength (related to proximity between visual elements). Through psychophysical experiments with texture discrimination tasks and computational modeling, they tested whether human performance follows patterns predicted by TWCO and whether perceptual learning enhances synchrony-based grouping.

We thank the reviewer for their thoughtful and constructive review. We believe the comments have served to improve our work.

Strengths:

(1) The theoretical framework connecting TWCO to visual perception is innovative and well-articulated, providing a potential mechanistic explanation for how gamma synchrony might contribute to both feature binding and separation.

(2) The methodology combines psychophysical measurements with computational modeling, with a solid quantitative agreement between model predictions and human performance.

(3) In particular, the demonstration that coupling strengths can be modified through experience is remarkable and suggests gamma synchrony could be an adaptable mechanism that improves with visual learning.

(4) The cross-validation approach, wherein model parameters derived from macaque neurophysiology successfully predict human performance, strengthens the biological plausibility of the framework.

Weaknesses:

(1) The highly controlled stimuli are far removed from natural scenes, raising questions about generalisability. But, of course, control (almost) excludes ecological validity. The study does not address the challenges of natural vision or leverage the rich statistical structure afforded by natural scenes.

We agree with the reviewer that the insights of the present study are limited to texture stimuli and have made adjustments in the Discussion (final two paragraphs) to avoid claiming generalizability to natural stimuli. We have also adjusted the title to specifically limit our results to texture stimuli. To establish the principles of TWCO, we needed tight control over the stimulus, but are intrigued by the idea to investigate natural scenes. We have added to our Discussion (paragraph 9) that future should evaluate to what extent the principles we investigate here apply to natural scenes. Synchrony-based mechanisms have been successfully used for image segmentation tasks in machine vision, showing that the proposed mechanism can in principle work for natural scenes.

(2) The experimental design appears primarily confirmatory rather than attempting to challenge the TWCO framework or test boundary conditions where it might fail.

We thank the reviewer for this important point. Our primary motivation was to address the neurophysiological properties of gamma synchrony that have been suggested to severely challenge the binding by synchrony mechanism. Particularly the strong dependence of gamma oscillations and synchrony on stimulus features. Our goal was to show that from the perspective of TWCO, these challenges become expected components of the mechanism. In essence, we wanted to promote a conceptual shift that converts what pushes a theory to its limit into something that is actually its central tenet. To facilitate this shift, we designed the experiment to directly test this core tenet.

While our approach was designed to test a central prediction of TWCO rather than explicitly challenge its boundaries, we respectfully argue that it was far from a simple confirmatory experiment. The design incorporated high-risk elements that provided considerable room for both the theory and our model to fail. First, the core prediction itself was non-obvious and highly specific. We did not simply test whether contrast heterogeneity and grid coarseness affect perception. We tested the stronger hypothesis that they would reflect a specific, interactive trade-off (the behavioral Arnold tongue) as specified by TWCO. Second, our modeling approach was deliberately constrained to provide a further stringent test. We did not post-hoc optimize the model's key parameters to fit our behavioral data. Instead, we fixed them a priori based on independent neurophysiological data from macaques. This was a high-risk choice, as a mismatch between a priori model predictions and the human data would have seriously challenged the framework's generalizability.

We agree that future research should further challenge TWCO. For instance, by using stimuli that require segregating several objects simultaneously or objects that cover more extensive regions of the visual field.

(3) Alternative explanations for the observed behavioral effects are not thoroughly explored. While the model provides a good fit to the data, this does not conclusively prove that gamma synchrony is the actual mechanism underlying the observed effects.

We agree that our results do not conclusively show that gamma synchrony is the actual mechanism underlying figure-ground segregation. We admit that the original phrasing used throughout the manuscript was too strong and gave the impression that we wanted to establish exactly that. However, the goal of our work was only to reinvigorate gamma synchrony as a potential contender by showing that features often cited as limitations of synchrony-based binding may in fact be essential properties of the mechanism. We have revised the title and made adjustments throughout the manuscript to better reflect this more moderate goal.

Additionally, we added tests of alternatives (Results, paragraphs 7–9) to clarify the unique explanatory value of the synchrony mechanism. To that end, we derived two alternative rate-based readouts from the same V1 simulations of our model. First, we extracted average firing rates inside the figure. Second, we computed the difference between average firing rates inside the figure and average firing rates in the background (rate difference). We analyzed each individually as predictors of behavior and performed a model comparison between these two and synchrony based on out-of-sample predictions. While the rate difference (but not average firing) showed meaningful associations with performance when considered alone, the synchrony readout had a larger effect size and was favored by the model comparison.

(4) Direct neurophysiological evidence linking the observed behavioral effects to gamma synchrony in humans is absent, creating a gap between the model and the neural mechanism.

We agree that the model only provides a how-possibly account linking stimulus features to performance. Showing that the brain actually relies on this mechanism would require showing that cortical synchrony mediates the effect of stimulus features on behavior beyond firing rates. Collecting such data would constitute a major effort that would go beyond the scope of this study. We acknowledge the need for electrophysiological data and the mediation analysis in the updated Discussion.

Achievement of Aims and Support for Conclusions:

The authors largely achieved their primary aim of demonstrating that human figure-ground perception follows patterns predicted by TWCO principles. Their psychophysical results reveal a behavioral "Arnold tongue" that matches the synchronization patterns predicted by their model, and their learning experiment shows that perceptual improvements correlate with predicted increases in synchrony.

The evidence supports their conclusion that gamma synchrony could serve as a viable neural grouping mechanism for figure-ground segregation. However, the conclusion that "stimulus-dependence of gamma synchrony is adaptable to the statistics of visual experiences" is only partially supported, as the study uses highly controlled artificial stimuli rather than naturalistic visual statistics, or shows a sensitivity to the structure of experience.

Likely Impact and Utility:

This work offers a fresh perspective on the functional role of gamma oscillations in visual perception. The integration of TWCO with perceptual learning provides a novel theoretical framework that could influence future research on neural synchrony.

The computational model, with parameters derived from neurophysiological data, offers a useful tool for predicting perceptual performance based on synchronization principles. This approach might be extended to study other perceptual phenomena and could inspire designs for artificial vision systems.

The learning component of the study may have a particular impact, as it suggests a mechanism by which perceptual expertise develops through modified coupling between neural assemblies. This could influence thinking about perceptual learning more broadly, but also raises questions about the underlying mechanism that the paper does not address.

Additional Context:

Historically, the functional significance of gamma oscillations has been debated, with early theories of temporal binding giving way to skepticism based on gamma's stimulus-dependence. This study reframes this debate by suggesting that stimulus-dependence is exactly what makes gamma useful for perceptual grouping.

The successful combination of computational neuroscience and psychophysics is a significant strength of this study.

The field would benefit from future work extending (if possible) these findings to more naturalistic stimuli and directly measuring neural activity during perceptual tasks. Additionally, studies comparing predictions from synchrony-based models against alternative mechanisms would help establish the specificity of the proposed framework.

Recommendations for the authors:

Reviewing Editor Comments:

In a joint discussion to integrate the peer reviews and agree on the eLife recommendations, both reviewers agreed that the work is valuable, but they were on the fence about whether the strength of evidence was incomplete or solid, eventually settling on incomplete. The reviewers make several recommendations for improving these ratings, which I (Reviewing Editor) have organised into 3 points below, with point 1 of particular importance. Underneath the summary, please see the individual recommendations of the reviewers.

(1) Strengthen evidence for the unique role of gamma synchrony in explaining the data, and ensuring claims are directly supported by relevant data:

Reviewers 2 and 3 both note the lack of direct evidence for gamma involvement, and reviewer 2 observes that the fit with behaviour may trivially be explained by a relationship between contrast heterogeneity and grid coarseness without need for oscillation. The reviewers felt that the approach of fitting the model to human data could be strengthened to help address this issue - and they offer various solutions, e.g., more principled a-priori criteria around good vs bad fit of the model to both main task and training data, and comparison to alternative binding models (Reviewer 2), identifying and testing boundary conditions of the model (Reviewer 3). There is also the possibility of collecting direct human neurophysiological evidence linking the behavioural data to neural mechanisms. Our discussion also highlighted the need to weaken claims (including in the title) where links are not directly demonstrated by methods from the present study, e.g., resting on indirect comparisons to primate literature.

We agree with the editor and reviewers that this was a critical point. To address it, we have made several major revisions.

As suggested, we have weakened claims where the links are not directly demonstrated by our data. The title has been revised to be more specific, and we have carefully edited the abstract, introduction, and discussion to distinguish between our model's predictions and direct neurophysiological evidence.

To address the concern that our model's fit might be trivially explained by visual features, we have performed a new analysis comparing the synchrony-based readout to two alternative rate-based readouts from the same V1 simulations. This new comparison shows that the synchrony readout provides a superior out-of-sample prediction of human behavior.

While a full implementation of a competing theory like "Binding by Enhanced Firing" would be a valuable next step, we note that parameterizing such a model in a comparably grounded framework is a substantial undertaking beyond the scope of the present study. Our new analysis provides an important first step in this direction.

(2) Make explicit and address the limitations of the stimuli:

Include that the model is not extracting the figure from the background, and the controlled stimuli may limit generalizability.

To address the concern that our model was not performing true figure-ground extraction, we performed a new set of simulations that included both the figure and the immediate background. The results confirm that synchrony dynamics within the figure region are not affected by the presence of the background. We added these validation results as supplementary materials. We have additionally made the modeling choice and its justification more explicit in the Results and Methods sections.

We have revised the Discussion to be more explicit about the limitations of using highly controlled texture stimuli. We now clearly state that our findings are specific to this context and that further research is required to determine if these principles generalize to the segregation of objects in natural scenes.

(3) Some clarifications to make more accessible:

Include the figure explaining the framework (Reviewers 1&2), and also the model details (Reviewer 2).

We have revised Figure 1 and its caption to more clearly illustrate the links from TWCO principles to their neural implementation in V1 and the resulting behavioral predictions.

We have expanded the Methods section to provide a more detailed and accessible description of the model's construction. We now clarify precisely how the oscillator grid was defined in visual space, how eccentricity-dependent receptive field sizes were implemented, and how these were mapped onto a retinotopic cortical surface to determine coupling strengths.

Reviewer #1 (Recommendations for the authors):

(A) Major concerns:

(1) My main concern:

My main concern is the repeated claims that the observed findings can be attributed to gamma synchrony in the early visual cortex. I find this claim misleading as the authors do not report any electrophysiological data that directly supports such claims. As stated in my public review, I feel that the authors should be clear about direct evidence versus more abstract inferences based on the literature.

In particular, I recommend changing claims about "gamma synchrony" to "Binding by Synchrony" That being said, the authors can outline that the model was built under the assumption that this synchrony is mediated by gamma in early visual cortex, but I don't think it should be part of their main conclusions.

We appreciate that TWCO’s general principles are frequency-agnostic and can be viewed as binding by synchrony in a broad sense. Our work, however, specifically instantiates these principles in V1 gamma: the model reflects TWCO dynamics together with V1 anatomy/physiology and the well-established contrast–frequency relationship in the gamma range (which, to our knowledge, has not been demonstrated with comparable specificity for other bands). In that sense, it is a gamma oscillator model of V1, rather than a generic BBS instantiation. Moreover, stimulus dependencies often cited as challenges to BBS have been used in particular to argue against gamma; showing that these very dependencies are integral to the TWCO mechanism is central to our contribution, and we therefore keep our conclusions focused on the gamma-specific instantiation tested here.

(2) Mediation of the observed effects by the visual features of the figure:

The authors motivate the hypothesis that BBS predicts that the perception of texture-defined objects depends on the density of texture elements and their contrast heterogeneity. This hypothesis seems trivial as those are the features that distinguish figure from ground. I think it would be important to clarify how this hypothesis is unique to BBS and not explained by competing theories, such as Binding by Enhanced Firing (Roelfsema, 2023). The authors should be clear about what part of the hypothesis is not trivial based on the task and clearly attributable to oscillators and synchrony.

Our stimulus features were derived from theory rather than psychophysical literature. Starting from the principles of TWCO, we mapped frequency detuning and coupling strength onto known anatomical and physiological properties of early visual cortex, and only then derived the corresponding stimulus manipulations (contrast heterogeneity and grid coarseness). We agree that grid coarseness (element distance) is an established facilitator of figure–ground perception. By contrast, contrast heterogeneity (feature variance) is less commonly emphasized as a figure–ground cue, compared to mean-based cues, but follows directly from TWCO’s frequency detuning. Importantly, mean contrast and luminance were matched exactly between figure and background in our stimuli. Demonstrating that contrast heterogeneity and grid coarseness not only independently affect figure-ground perception, but reflect a trade-off where higher heterogeneity needs to counteracted by reduced grid coarseness in the way TWCO specifies is therefore non-obvious and provides an initial empirical indication that the core TWCO variables might shape perception. We also agree that alternative models would further clarify the unique explanatory value of synchrony. In the revised manuscript, we compare rate-based readouts (mean figure rate; figure–background rate difference) with the synchrony readout from the same simulations. Rate difference indeed constitutes a predictor of performance, but the synchrony readout showed a larger effect and was preferred by out-of-sample model comparison.

Using a linear model, the authors assess the relationship between discrimination accuracy and synchrony. Did the authors also include the factors grid coarseness and contrast heterogeneity in this model? Again, as both the task performance (as shown by the GEE analysis) and oscillatory synchrony depend on these features, the relationship between model and behavioral performance will be mediated by the visual features.

Thank you for raising this. In our framework, detuning (via contrast heterogeneity) and coupling (via grid coarseness) are the inputs, synchrony is the proposed mechanistic mediator, and behavior is the output. Because synchrony in our model is a (near-)deterministic function of the manipulated features under fixed parameters, a joint features+synchrony regression is statistically ill-posed (perfect multicollinearity up to numerical error) and cannot add information. A proper mediation test would require trial-wise neural measurements of synchrony in the same task, which we do not have and acknowledge as a limitation in the Discussion. Accordingly, we show that both the features themselves (reflecting TWCO principles) and model-derived synchrony (realizing the proposed pathway) account for behavior.

We agree this does not establish a unique contribution of synchrony. To probe alternatives, we added rate-based readouts and a model comparison to the revised manuscript. These additional analyses indicate that synchrony outperforms simple rate-based mappings. We do not claim this rules out more sophisticated rate-based mechanisms. Our aim is to demonstrate that synchrony is a viable, behaviorally informative readout for downstream processing. We do not assert it is the only mechanism the brain uses. Synchrony had been discounted due to its stimulus dependence; our results are intended to rule it back in. We have made changes throughout the manuscript to better reflect this more modest aim.

(3) Goodness of fit measures are not established a prior:

I have described this concern in my public review. It is hard to assess what the authors would have interpreted as a good or a bad fit, especially without accounting for the confound in the relationship between oscillator synchrony and behavior. Similarly, when assessing the similarity between the behavioral and dynamic Arnold Tongues across different coupling parameters, the authors found that the chosen parameters (based on macaque data) were not optimal. They offer the explanation that the human cortex has a lower coupling decay than the macaque cortex, and the similarity is higher for lower values of coupling decay. While this explanation is not entirely implausible, it is unclear where an oscillator model with human values would be in the presented plot, as the authors didn't estimate those values from the human studies. Moreover, the task used in the Lowet et al., 2017 paper is very different from the task presented here, which could also account for differences. Overall, the explanation appears hand-wavy considering the lack of empirically defined goodness of fit measures.

Thank you for these concerns.

We did indeed not provide a priori thresholds for what would be considered good fit. Instead, we used two complementary benchmarks; namely noise ceilings and parameter exploration. The former provides an upper bound on what any model (not just ours but based on completely different mechanisms) could achieve given our data. The parameter sweep provides an indication how well our concrete model can maximally fit the data and how bad it can be based on possible parameters. These benchmarks are more informative than a fixed a-priori cutoff, which would depend on unknown noise and inter-subject variability. Both the noise ceiling and the parameter exploration indicate that our model, using a priori fixed parameters, performs well. Additionally, we redid all our statistical analyses after z-normalizing every predictor to provide easier interpretation of effect sizes.

Regarding the reason that key model parameters were not optimal, we believe our interpretation to be plausible. We agree that we currently do not have data to estimate the exact human decay factor and hence cannot establish how much model fit would be affected. However, the parameter exploration in Figure 3 shows that small to modest reductions in decay would improve model fit. We discuss this now in the revised manuscript.

The reviewer’s suggestion is intriguing. While Lowet et al. (2017) used a different task, the parameters we took from their work (decay rate and maximum coupling) are intended to reflect anatomical properties and thus should not be task-dependent. That said, Lowet et al. ‘s data carry uncertainty, so our estimates may not be exact; we note this explicitly in the revised Discussion. Whether a different task would have yielded better parameter estimates is difficult to determine, but we considered Lowet’s paradigm appropriate because it was designed to target the same V1 anatomical and physiological properties that map onto TWCO.

I have concerns about a similar confound in the training effects. If I'm not mistaken, the Hebbian Learning rule encourages synchronization between the oscillators in the grid. As such, it causes synchronization to increase over several simulations. Clearly, the task performance of the participants also improves over the sessions. Again, an empirical threshold would be required to assess whether the similarity in learning between model and performance goes beyond what is expected based on learning alone. How much of these effects can be attributed to the model being oscillatory?

The reviewer is correct that, in our framework, learning operates via changes in coupling that increase synchrony. Enhanced synchrony is the proposed (and in our model also the actual) pathway by which learning impacts behavior. We agree that learning could, in principle, act through pathways other than synchrony. Demonstrating this would not be achieved by a mediation analysis here, because that requires independent, trial-level neural measurements of the candidate pathways (synchrony and alternatives). In the absence of such data, the appropriate approach would be model comparison between competing mechanistic readouts. We have added such a model comparison for a synchrony readout versus two rate-based readouts derived from the same simulations for the first session; i.e., focusing on the pathway from stimulus features to behavior. However, a similar model comparison is not possible for learning. As we show in the supplementary materials, rate-based readouts of our V1 model are not at all affected by coupling strength. As such, they are insensitive to changes in coupling and are thus not viable as alternative mechanisms to explain performance changes due to learning. A fair test of rate-based alternatives would require building a detailed rate-based figure–ground segregation model that predicts session-wise changes. We agree that this is an important next step but it is also substantial undertaking beyond the scope of the present study.

(4) Similarly, for the comparison of the Arnold Tongue in the transfer session and the early session:

In the first part of the Results section, it says: "Our model rests on the assumption that learning-induced structural changes in early visual cortex are specific to the retinotopic locations of the trained stimuli. We evaluated whether this assumption holds for our human participants using the transfer session following the main training period. [...] If learning is indeed local, participants' performance in the transfer session should resemble that of early training sessions, indicating a reset in performance for the new retinal location."

The authors find that a model fit to session 3 explains the data in the transfer session best and consider this as evidence for the above-stated expectation. Again, it is unclear where the cutoff would have been for a session to be declared as early or late. For instance, had the participants only performed 4 sessions, would the performance be best explained by session 3 or session 1?

A high number of statistical tests are used, which, firstly, need to be corrected for multiple comparisons (did the authors do this?). Secondly, I feel that the regression models could be improved. For instance, the authors fit one model per session and then assess how well each model explains the variance in the transfer session. I think the authors might want to opt for one model with the regressors contrast heterogeneity, grid coarseness, and session (and their interaction). Using this approach, the authors would still be able to assess which session predicts the data best. Similarly, interindividual variability could be accounted for by adding participant-specific random effects to the model (and using a mixed model), instead of fitting individual models per participant.

We agree the “early vs late” cutoff was underspecified. In the revision, we predefine Session 2 as the early-learning reference, excluding Session 1 to avoid familiarization/response–mapping effects. We then fit a single Bayesian hierarchical model with contrast heterogeneity, grid coarseness, and session, plus a transfer indicator, and participant-level random effects. This allows us to place the transfer session on the same scale as training and to test a) whether the transfer session precedes the state in session 2 via the posterior contrast P(βtransfer<βSess2) and b) whether it is indistinguishable from the state in session two using an equivalence test derived from the fitted model. We find that the transfer session is equivalent to session 2. We added this updated analysis of the transfer session in the Results (paragraph 15).

In response to the suggestion to use a hierarchical regression model for analyzing the transfer session, we have decided to use such a model for all our analyses in a Bayesian framework. In this Bayesian framework, inference is based on the joint posterior (credible intervals/equivalence) of all predictors in a model and additional post-hoc multiplicity corrections are not required.

(5) Questions regarding the model:

What does it mean that the grid was "defined in visual space"? How biologically plausible with regard to the retinotopy and organization of the oscillators do the authors claim the model to be?

We are happy to clarify this point. We have a total of 400 oscillators reflecting neural assemblies in V1. We start by defining a regular, 20x20, grid of the receptive field (RF) centers of these oscillators inside the figure region. Each oscillator is then also assigned a RF size based on the eccentricity of its RF center. We use the threshold-linear relationship between RF eccentricity and RF size reported in [1] to assign RF sizes. Each oscillator thus has an individual, eccentricity-dependent, RF size.

For the coupling between oscillators, we need to know their cortical distances. We obtain these by first determining the cortical location of each oscillator through a complex-logarithmic topographic mapping of neuronal receptive field coordinates onto the cortical surface [2,3]. For this mapping, we use human parameter values estimated by [4]. From these cortical locations, we then compute pairwise Euclidean distances.

The model thus captures realistic retinotopy, eccentricity-dependent RF sizes, and distance-dependent coupling on the cortical surface. We have adjusted our Methods to make these steps clearer.

(1) Freeman, J., & Simoncelli, E. P. (2011). Metamers of the ventral stream. Nature neuroscience, 14(9), 1195-1201.

(2) Balasubramanian, M., & Schwartz, E. L. (2002). The isomap algorithm and topological stability. Science, 295(5552), 7. https://doi.org/10.1126/science.1066234

(3) Schwartz, E. L. (1980). Computational anatomy and functional architecture of striate cortex: a spatial mapping approach to perceptual coding. Vision Research, 20(8), 645–669. http://www.sciencedirect.com/science/article/pii/0042698980900905

(4) Polimeni, J. R., Hinds, O. P., Balasubramanian, M., van der Kouwe, A. J. W., Wald, L. L., Dale, A. M., & Schwartz, E. L. (2005). Two-dimensional mathematical structure of the human visuotopic map complex in V1, V2, and V3 measured via fMRI at 3 and 7 Tesla. Journal of Vision, 5(8), 898. https://doi.org/10.1167/5.8.898

Similarly, do the authors claim that each gabor annuli stimulates a single receptive field in V1?

We hope that with the additional explanation above, it is clearer that there is not a one-to-one mapping. Each oscillator samples the local image by pooling over all Gabor annuli that overlap its receptive field (partially or fully) and computes the average contrast within its RF. Conversely, a single annulus typically overlaps multiple RFs and contributes to each in proportion to the overlap.

I am unsure how the oscillators were organized, if not retinotopically. How is the retinotopic input fed into the non-retinotopically arranged oscillators?

We hope that with the additional explanation above, it is clearer that the network is strictly retinotopic.

The frequency of each oscillator changes according to ω=2πv with ν=25+0.25C. How were the values for the linear regression in v chosen? Reference?

The slope and intercept parameters for this equation were first reported in [5]. We added the reference to the Methods.

(5) Lowet, E., Roberts, M., Hadjipapas, A., Peter, A., van der Eerden, J., & De Weerd, P. (2015). Input-dependent frequency modulation of cortical gamma oscillations shapes spatial synchronization and enables phase coding. PLoS computational biology, 11(2), e1004072.

(6) Hebbian Learning Rule:

I am confused about how the effective learning rate E= ∈t is calculated. It is said that it is estimated based on the similarity between the second experimental session and the distribution of synchrony after letting the model learn. How can the model learn without knowing epsilon and t?

We agree with the reviewer that our procedure to estimate the effective learning rate requires further clarification. We performed a nested grid search. Essentially, we let the model learn between session 1 and 2 with each of 25 candidate effective learning rates and evaluate how well each of them allow the model to fit performance in session 2. We then select the best effective learning rate and create a new, smaller, grid around this value and repeat that procedure. In total we perform 5 nested grids to arrive at the final effective learning rate. We expanded the explanation in the Methods.

(B) Minor concerns:

(1) Small N: 2/3 of the studies that were cited to justify the small sample were notably different from the current experiment, i.e., Intoy 2020 is an eye movement task, Lange 2020 is a memory task (Tesileanu 2020 is more similar). I think a power analysis would be great to support, as the sample size seems quite low

Our study uses a within-subject design with ~750 trials per session (≈6,000 total) per participant, analyzed with a hierarchical model that pools information across trials and participants. To assess adequacy, we ran a simulation-based design analysis using the fitted hierarchical model (i.e., post hoc, based on the observed variance components). This analysis indicated a detection probability >90% for all key effects. We now report the results of this design analysis in the (Supplementary Table 1) and note this in the Results (paragraph 1).

Regarding the literature context, we agree the cited studies are not identical to ours; we referenced them to illustrate a common practice (small N with many trials) when targeting low-level, early-visual mechanisms. Intoy (pattern/contrast sensitivity) and Lange (perceptual learning in early vision) share that focus, while Tesileanu is methodologically closest.

(2) Figure 1 could be more informative and better described in the text. The authors often don't refer to the panels in Figure 1. Maybe it would help to swap a and b to describe the Arnold tongue first? It might also be a good idea to add the coupling strength and frequency detuning axes

We have swapped panels a and b and now refer to each panel in the main text to enhance clarity.

(3) Values of rho (distance - is this degrees visual angle)? Do the authors assume that the size of the stimuli corresponds to receptive fields in V1? If so, how is this justified?

The center-to-center distance between any pair of neighboring annuli is indeed expressed in degrees of visual angle. Rho is a scaling factor for this distance. With rho=1, the center-to-center distance corresponds to the diameter of the annuli; i.e., they touch but do not overlap each other. We do not assume any relation between the size of receptive fields and the size of the annuli. Receptive field sizes in our model are purely determined by their eccentricity and each oscillator can have several annuli within its receptive field while each annulus can fall within several overlapping receptive fields of different oscillators. We believe that the schematic illustration in Figure 1 might have given the impression that each oscillator sees exactly one annulus and added a note that this is not the case and merely an oversimplification to illustrate the relationship between contrast and intrinsic frequency.

(4) Some equations are embedded in the text, and some are not. It might be easier to find the respective equation if they all have an index. For instance, the authors mention the psychometric function that relates model synchrony and performance in the results section. It would be easier to find if it had an index that the authors could refer to.

We moved this equation as well as the contrast intrinsic frequency mapping from inline to displayed and numbered them.

(5) Is there a reference for "Our model rests on the assumption that learning-induced structural changes in early visual cortex are specific to the retinotopic locations of the trained stimuli"? (If so, it should be cited.)

We added references supporting this assumption.

(6) Figure 2b: colorbar missing label.

We added the label.

Reviewer #2 (Recommendations for the authors):

Cool work!

(1) The reader would benefit from (a single) comprehensive figure that visually explains the entire conceptual framework-from TWCO principles to neural implementation to behavioural predictions-accessible to readers without specialised knowledge of oscillatory dynamics. This will give the paper a greater impact.

We have adjusted Figure 1 in accordance with suggestions made by reviewer 1 and added further explanations to the caption and the Introduction to enhance clarity on how the principles of TWCO relate to neural implementation.

(2) I think this paper would benefit from the audience eLife provides, but the paper could move closer to the audience.

(3) Pride comes before the fall, but I am not the most uninformed reader, and it took me some effort to process everything.

Thank you, we took this to heart. In the Introduction, we now state more explicitly how each variable is operationalized and how these map onto TWCO with improved reference to relevant panels in the schematic figure. We agree the framework is conceptually dense. TWCO principles reach the stimuli through specific V1 anatomy and physiology, so there are several links to keep in mind. Our goal with the revised introduction and figure is to make those links better visible.

(4) You could consider discussing potential implications for understanding perceptual disorders characterized by altered neural synchrony (e.g., schizophrenia, autism) and how your learning paradigm might inform perceptual training interventions.

Thank you for this suggestion. We have added that TWCO might provide a new lens to study perceptual disorders to the Discussion. We provide a concrete example of the relation between grouping, gamma synchrony (in light of TWCO) and lateral connectivity in schizophrenia

(5) I think this paper has real strength, but rather than dispersing limitations throughout the discussion, create a dedicated section that systematically addresses ecological validity, alternative explanations, and generalisability concerns. This will also preempt criticism.

We appreciate the suggestion. Our preference is to discuss limitations in context, next to the specific results they qualify, so readers see why each limitation matters and how it affects interpretation. Nevertheless, paragraph 7 on page 20 summarizes most limitations in a single paragraph.

That sentence is definitely worded in a slightly confusing way! To make it clearer, think of it as a "Safety Threshold."

In simple terms, it describes the tipping point for herd immunity.

Breaking it down

The text says $\chi^* = \frac{1}{R_0}$. Here is what that actually represents:

1. The Threshold ($\chi^*$): This is the specific proportion of the population that is still susceptible (not immune).
2. The "Safety" Rule: To avoid an epidemic, the actual proportion of susceptible animals in your population must stay below this $\chi^*$ number.
3. The "0" in the text: The text has a small typo or awkward phrasing where it says "which is 0 the maximum..." It likely meant to say "which is the maximum proportion."

Why $1/R_0$ matters

The Basic Reproductive Number ($R_0$) tells you how many new cases one infected animal will cause.

• If $R_0 = 4$, then $\chi^ = 1/4 = \mathbf{0.25}$ (or 25%*).
• This means if more than 25% of your animals are susceptible, the disease will spread (an epidemic).
• If fewer than 25% are susceptible (meaning 75% are immune/vaccinated), the disease will die out because the "effective" reproductive number drops below 1.

A clearer rewrite of that sentence:

"This value ($\chi^$) represents the maximum allowed proportion* of susceptible animals. If the population's actual susceptibility stays at or below this limit, a disease with a reproductive power of $R_0$ cannot start an epidemic."

In your research context

Since you are looking at epidemiology at BNITM, this formula is the foundation for deciding vaccination targets. If you know the $R_0$ of a disease is 5, you know you must vaccinate until the susceptible proportion is less than $1/5$ ($20\%$).

Difference between proportion and ratio:

1. The "Part-to-Whole" vs. "Part-to-Part" Rule

   Proportion (Part-to-Whole): The numerator is "inside" the denominator. You are comparing a slice to the entire pizza.

   Logic: A+BA​
   
   Example: If you have 2 female researchers and 8 male researchers, the proportion of females is 2/10 (or 0.2).
   

   Ratio (Part-to-Part): The numerator is "outside" the denominator. You are comparing one distinct group to another distinct group.

   Logic: BA​
   
   Example: Using the same group, the ratio of females to males is 2/8 (or 1:4).
   

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Referee #3

Evidence, reproducibility and clarity

Velázquez et al. investigate the transcriptomic and epigenetic consequences of exogenous expression of the Ewing sarcoma fusion oncogene EWSR1∷FLI1 (EF1) in yeast. The study provides compelling evidence that EF1 can bind ETS transcription factor motifs, as well as a single 4xGGAA repeat within the S. cerevisiae genome, despite the absence of several canonical cofactors often implicated in EF1 biology, including CBP/p300 and Polycomb group (PcG) proteins. The authors further show that EF1 expression redistributes RNA Polymerase II toward EF1-bound ETS sites, yet. Strikingly, this relocalization is accompanied by only modest global transcriptional effects relative to those reported in human or insect systems. In addition, EF1 expression reverses repeat-associated epigenetic silencing of synthetic GGAA microsatellites in engineered reporter strains. Taken together, the data support the conclusion that GGAA microsatellite-mediated transcriptional rewiring is a comparatively conserved EF1 property, whereas broader transcriptomic changes arising from individual EF1-bound ETS sites appear to be more context-dependent. Overall, the manuscript is clearly written and logically organized, and the methodological descriptions and data-analysis details appear sufficient to enable reproducibility.

Major comments

None.

Minor comments

1. Additional citations in the Introduction. A small number of additional references would further support specific statements.
   • End of paragraph 3: consider adding Boulay et al. (2017).
   • Paragraph 4, after "proximal and distal genes": consider adding Tomasou et al. (2015) and Orth et al. (2022).
2. Potential antibody cross-reactivity in the CoIP experiment. Is there an EWSR1 homolog in S. cerevisiae? To rule out unintended interactions, it would be helpful to exclude binding of endogenous yeast proteins by the anti-EWS antibody used for co-immunoprecipitation, for example via a homology search and/or appropriate specificity controls.
3. Clarification of EF1-associated toxicity. The authors suggest that part of the observed transcriptional signal may reflect EF1 toxicity. It would strengthen the interpretation to characterize this phenotype more explicitly (e.g., growth rate over time, viability/cell death, or longer-term fitness effects). In addition, it would be informative to test whether toxicity depends on EF1 DNA-binding activity and whether truncation mitigates toxicity, as reported in Drosophila (Mahnoor et al., 2024).
4. RNA Polymerase II relocalization versus limited transcriptional output. The apparent recruitment/repositioning of RNA Pol II in the absence of substantial transcriptional change is particularly interesting. This point could be strengthened by assessing RNA Pol II "states," for example using phosphorylation-state specific antibodies to distinguish stalled/paused from actively elongating polymerase.
5. Promoter choice in the GGAA microsatellite reporter. The use of a modified constitutive promoter to monitor GGAA microsatellite-dependent activation is somewhat unconventional. Many studies (e.g., Gangwal et al., Hölting et al.) use minimal promoters to demonstrate EF1-dependent upregulation rather than reversal of heterochromatin-associated silencing. A brief rationale for the chosen design or discussion of how it relates to prior reporter paradigms would help readers contextualize the approach.
6. Reconstituting minimal cofactor requirements for ETS-site activity. The finding that EF1 binding at single ETS sites does not translate into strong transcriptomic remodeling in yeast is an intriguing aspect of the work. The manuscript could be further enriched by systematic attempts to reconstitute candidate cofactors in this minimal system to define the minimal requirements for ETS-site-dependent gene activation.

Significance

This study will be of broad interest because it convincingly separates EF1-driven GGAA microsatellite-dependent activation from the canonical regulatory functions of FLI1, reinforcing the concept that fusion transcription factors can acquire genuinely neomorphic activities-activities that may ultimately be therapeutically actionable. Beyond the biological insight, the successful establishment of exogenous EF1 expression in yeast is itself a notable technical achievement, given the longstanding challenges associated with EF1 expression in heterologous settings. As presented here, yeast offers a valuable platform to interrogate EF1 function in a simplified and more controlled context.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer 1 (Public review):

When do behavioral differences emerge between the task variants? Based on the results and discussion, the cues increase the salience of either the wins or the losses, biasing behavior in favor of either risky or optimal choice. If this is the case, one might expect the cues to expedite learning, particularly in the standard and loss condition. Providing an analysis of the acquisition of the tasks may provide insight into how the cues are "teaching" decision-making and might explain how biases are formed and cemented.

While considerable differences in decision making emerge in early sessions of training, we do not observe any evidence that cuing outcomes expedites the development of stable choice patterns. Indeed, since the outcomes are cued across all four options, there is no categorical difference in salience between optimal and risky choices. Thus, our interpretation is that cuing wins and/or losses alters the integration of this feedback into choice preference, rather than the rate of the development of choice preference. To quantitatively address this point, we have included the following analysis:

“To quantitatively examine choice variability during training, we binned sessions 1-5 and 6-10 and analyzed variability in choice patterns across task variants. Analysis of the first five sessions of training revealed a significant shift in decision score across sessions (F(3, 502) = 31.23, p <.0001), which differed between task variants (session x task: F(16, 502) = 2.13, p = .007). Conversely, while significant differences in overall score were observed between task variants in sessions 6-10 (task: F(5, 156) = 6.81, p <.0001), there was no significant variability across sessions (session: F(3, 481) = 2.06, p = .10, task x session: F(15, 481) = 0.78, p = .71). This indicates that the variability in choice preference (and presumably, learning about outcomes) is maximized in the first five sessions, and there are no obvious differences in the rate of development of stable choice patterns between task variants.”

Does the learning period used for the modeling impact the interpretation of the behavioral results? The authors indicate that computational modeling was done on the first five sessions and used these data to predict preferences at baseline. Based on these results, punishment learning predicts choice preference. However, these animals are not naïve to the contingencies because of the forced choice training prior to the task, which may impact behavior in these early sessions. Though punishment learning may initially predict risk preference, other parameters later in training may also predict behavior at baseline.

The first five sessions were chosen based on a previously developed method used in Langdon et al. (2019). When choosing the number of sessions to include, there is a balance between including more data points to improve estimation of parameters while also targeting the timeframe of maximal learning. As training continues, the impact of outcomes on subsequent choice should decrease, and the learning rate would trend towards zero. This can be observed in the reduction in inter-session choice variability as training progresses, as demonstrated in the analyses above. Once learning has ceased, presumably other cognitive processes may dictate choice (for example, habitual stimulus-response associations), which would not be appropriately captured by reinforcement learning models. It would be a separate research question to determine the point at which parameters no longer become predictive, requiring a larger dataset to thoroughly assess. We acknowledge that we did not provide sufficient justification for the learning period used for the modeling. In conjunction with the analysis of early sessions outlined above, we have added the following to the text:

“We investigated differences in the acquisition of each task variant by fitting several reinforcement learning (RL) models to early sessions. Our modeling approach closely follows methods outlined in Langdon et al. (2019), in which a much larger dataset (>100 rats per task) was used to develop the RL models applied here. Due to the comparatively small n per group in the current study, we limited our model selection to those previously validated in Langdon et al. (2019), with minor extensions. As in previous work, models were fit to valid choices from the first five sessions. As training continues, the impact of outcomes on subsequent choice should decline, and parameter values may evolve over time (e.g., decreasing learning rate). To target the period of learning during which outcomes have maximal influence over choice, and parameters likely have fixed values, we limited our analyses to the first five sessions.”

The authors also present simulated data from the models for sessions 18-20, but according to the statistical analysis section, sessions 35-40 were used for analysis (and presumably presented in Figure 1). If the simulation is carried out in sessions 35-40, do the models fit the data?

Based on our experience, choice patterns are well instantiated by session 20, and training only continues to 30+ sessions to achieve stability in other task variables (e.g., latencies, premature responding, etc.). That being said, the discrepancy between session numbers is confusing, so we’ve extended the simulations to match the same session numbers that were analyzed in the experimental data.

Finally, though the n's are small, it would be interesting to see how the devaluation impacts computational metrics. These additional analyses may help to explain the nuanced effects of the cues in the task variants. 

Unfortunately, as the devaluation experiment is only one session, there are insufficient data to run the same models. Furthermore, changes in choice are subtle and not uniform across rats, making it difficult to reliably model this effect at the individual level. A separate experiment could investigate the specific cognitive processes underlying the devaluation effect.

Reviewer #1 (Recommendations for the authors):

The authors do not present individual data points for behavior. Including these data points would improve the interpretability of the results. Adding significant notations to the bar graphs would also help the reader. Although the stats are provided and significant comparisons highlighted, it isn't easy to go between the table and the figure to detect significant outcomes. If done, the statistics tables could be moved to the supplement. Including estimates of effect size for main findings in the main text would also benefit the reader. 

We thank the reviewer for their feedback on our approach to the figures and significance reporting – we have updated the relevant figures to include individual data points. Furthermore, we’ve added significance notations for task variants that are significantly different from the uncued or standard cued tasks on the figures. We’ve also moved some statistics tables to the supplement, as suggested. 

The authors allude to other metrics of the task (trials, omissions, etc.) but do not present these data anywhere. Including supplementary figures including individual data points and statistical analyses in the supplement is strongly encouraged.

A supplementary figure visualizing these metrics (choice latency, trials completed, and omissions) has been added, with individual data points included. Statistical analyses are reported in the main text – no significant effect in the ANOVAs were observed for any of these metrics, so post hoc analyses were not performed. 

Figure 4 is confusing. Presenting the WAIC values for each model rather than compared to the nonlinear model would be easier to understand. It is also unclear if statistical tests were used to assess differences in model fit as no test information is provided.

Figure 4 has been updated to increase clarity and address feedback from another reviewer. Raw WAIC values are not ideal for visualization, as the task variants have differing amounts of data and thus would be difficult to include on the same Y-axis. Instead, we present each model’s difference in WAIC relative to a basic model with no timeout penalty transform, so that all three models are visible, and the direction of model improvement is clearly indicated. Statistical tests of WAIC differences are not standard, as the numerical differences themselves indicate a better fit.

The authors do not provide a data availability statement.

We thank the reviewer for calling our attention to this oversight. A data availability statement has been added. 

Reviewer 2 (Public review):

Additional support and evidence are needed for the claims made by the authors. Some of the statements are inconsistent with the data and/or analyses or are only weakly supportive of the claims.

We appreciate the reviewer’s overarching concern that some claims in the original manuscript were insufficiently supported by the data or analyses. To address this, we have provided further rationale for the devaluation experiment and clarified our interpretation of those results, expanded the computational modeling analyses, and revised figures and wording to improve clarity. Below, we respond to the reviewer’s specific comments in detail.

Reviewer #2 (Recommendations for the authors):

Different variants of an RL model were used to understand how loss outcomes impacted choice behavior across the gambling task variants. Did the authors try different variants for rewarded outcomes? I wonder whether the loss specific RL effects are constrained to that domain or perhaps emerged because choice behavior to losses was better estimated with the different RL variants. For example, rewarded outcomes across the different choices may not scale linearly (e.g., 1, 2, 3, 4) so including a model in which Rtr is scaled by a free parameter might improve the fit for win choices.

We agree that asymmetries in model flexibility could, in principle, contribute to the observed effects. While we are somewhat limited in our ability to develop and validate further models due to the small size of the datasets compared to the high degree of choice variability between rats, we have explored the possibility as far as the data allow by fitting a model that includes a scaling parameter for rewards in addition to punishments:

“While we restricted our model selection to those previously validated on larger datasets, the specificity of the main finding to the punishment learning rate may be due to the greater flexibility afforded to loss scaling, rather than a true asymmetry in learning. To test this hypothesis, we fit a model featuring a scaling parameter for rewards, in addition to scaled costs:

where mRew is a linear scaling parameter for reward size. A separate scaling parameter was used for timeout penalty duration (i.e., same as scaled cost model). Group-level parameter estimates (Figure S3) reflected similar differences in the punishment learning rate and reward learning rate as the scaled cost model (Figure S4). Furthermore, all 95% HDIs for the mRew scaling parameter included 1, indicating that at least at the group level, scaling of reward size across the P1-P4 options closely follows the actual number of earned sucrose pellets. Thus, we find no evidence that our results can be simply attributed to the increased parameterization of losing outcomes.”

Additionally, I would like to see evidence that these alternative models provide a better fit compared to a standard delta-rule updating for unrewarded choices.

Each model is now compared directly to a standard delta-rule update model in the WAIC figure to demonstrate that the current models are a better fit for the data.

Could the authors provide some visualization of how variation in the r, m, or b parameters impact choices and/or patterns of choices?

We have added a figure to the supplementary section to visualize how different values for the r, m, and b parameters could alter the size of updates to Q-values on each trial across the four different options, thereby impacting subsequent choice. 

It was challenging to understand the impact of the reported effects and interpretation of the authors at various points in the manuscript. For example, the authors state that "only rats trained on tasks without win-paired cues exhibited shifts in risk preference following reinforcer devaluation". Figure 3 however seems to indicate that rats trained on the reverse-cued task show shifts in risk preference. 

We agree the original wording did not fully capture the nuance apparent in the figure. While not significantly different from baseline, rats in the reverse-cued experiment could have indeed updated their choice patterns and we were underpowered to detect the effect. We have updated the results section to include this point, and to more specifically outline that win-paired cues that scale with reward size lead to insensitivity to reinforcer devaluation:

“This indicates that pairing audiovisual cues with reward induces some degree of inflexibility in risk-preferring rats. Importantly, pairing cues with losses alone does not elicit rigidity in choice. Thus, in keeping with the observed effect on overall choice patterns, pairing cues with wins has a unique impact on sensitivity to reinforcer devaluation. Although not statistically significant, visual inspection of the reverse-cued task suggests that some choice flexibility may be present, and the study may be underpowered to detect this effect. Nonetheless, win-paired cues that scale with reward size reduce flexibility in choice patterns following reinforcer devaluation.”

It was not clear to me why the authors did a devaluation test and what was expected. Adding details regarding the motivation for specific analyses and/or experiments would improve understanding of these exciting results.

Further explanation has been added to the results section for the devaluation test to clarify the rationale and expected results:

“We next tested whether pairing salient audiovisual cues with outcomes on the rGT impacts flexibility in decision making when outcome values are updated. Reinforcer devaluation, in which subjects are sated on the sugar pellet reinforcer prior to task performance (presumably devaluing the outcome), is a common test of flexibility of decision making (Adams & Dickinson, 1981). We have previously employed this method to demonstrate that rats trained on the standard-cued task are insensitive to reinforcer devaluation (i.e., choice patterns do not shift despite devaluation of the sugar pellet reward; Hathaway et al., 2021).”

Some rats in the rGT become risk takers and some do not, but whether this is an innate phenomenon or emerges with training is not known. The authors report some correlations between the RL parameters and subsequent risk scores but this may be an artifact because the risk scores and many of the parameters differ between the experimental groups. Restricting these analyses to the rats in the standard procedure (or even conducting it in other rats that have been run in the rGT standard task) would alleviate this concern. The authors should also expand upon this result in the discussion. (if it holds up) and provide graphs of this relationship in the manuscript.

In a previous paper on which these analyses were based (Langdon et al., 2019), analyses of the relationship between RL parameter estimates and final decision score were conducted separately for rats trained on either the uncued or standard cued task, as the reviewer has suggested here. Those analyses showed that parameters controlling the learning from negative outcomes were specifically related to final score in both tasks. While we don’t have the appropriate n per group to split the analyses by task variant in the current study, we have highlighted these previous findings in the results section to address this concern:

“In Langdon et al. (2019), analyses were conducted to test whether parameters controlling sensitivity to punishment predicted final decision score at the end of training in the uncued and standard cued task variants. These analyses showed that across both task variants, there was evidence of reduced punishment sensitivity (i.e., lower m parameter or punishment learning rate) in risky versus optimal rats. We conducted similar analyses here to examine whether parameter estimates covary with decision score at end of training. To accomplish this, we fit simple linear regression models for each parameter and assessed whether the slopes were significantly different from zero.”

I don't see a b parameter in the nonlinear cost model, but is presented in Figure 6 and also in the "Parameters predicting risk preference on the rGT". The authors either need to update the formula or clarify what the b parameter quantifies in the nonlinear model.

We thank the reviewer for pointing out this oversight; the equation has been updated to include the b parameter.

The risk score is very confusing as high numbers or % indicate less risk and lower (more negative numbers) indicate greater risk. I've had to reread the text multiple times to remind myself of this, so I anticipate the same will be true for other readers. Perhaps the authors can add a visual guide to their y-axis indicating more positive numbers are less risky choices.

We acknowledge that this measure can be confusing – the calculation of this score is standard for the Iowa Gambling Task conducted in humans, on which the rGT is based, and was therefore adopted here. We’ve changed the name from “risk score” to “decision score”, along with including a visual guide to the y-axis in Figure 2, to address this point.

Negative learning rate is confusing as it almost implies that the learning was a negative value, rather than being a learning rate for negative outcomes. Please revise in the figures and in the text.

We have updated the text and figures where appropriate from “negative learning rate” to “punishment learning rate”. We have also changed the text from “positive learning rate” to “reward learning rate” to match this terminology.

Reviewer 3 (Public review):

There is a very problematic statistical stratagem that involves categorising individuals as either risky or optimal based on their choice probabilities. As a measurement or outcome, this is fine, as previously highlighted in the results, but this label is then used as a factor in different ANOVAs to analyse the very same choice probabilities, which then constitutes a circular argument (individuals categorised as risky because they make more risky choices, make more risky choices...).

Risk status was included as a factor to test whether the effects of the cue paradigms differed between risky versus optimal rats (i.e., interaction effects), not as an independent predictor of choice preference. We focus on results showing a significant task x risk status interaction, and conducted follow-up analyses separately within each group, at which point risk status was no longer included as a factor. We do not interpret main effects or choice x status interactions, which would indeed be circular for the reason noted by the reviewer.

A second experiment was done to study the effect of devaluation on risky choices in the different tasks. The results, which are not very clear to understand from Figure 3, would suggest that reward devaluation affects choices in tasks where the win-cue pairing is not present. The authors interpret this result by saying that pairing wins with cues makes the individuals insensitive to reward devaluation. Counter this, if an individual is prone to making risky choices in a given task, this points to an already distorted sense of value as the most rewarding strategy is to make optimal non-risky choices.

We have included significance notations in Figure 3 and included further detail in the text to improve clarity of the findings for the devaluation test. The reviewer raises an interesting point that risk-preferring rats have a distorted sense of value, since they do not follow the optimal strategy. However, we believe that this is at least partially separable from insensitivity to devaluation, since risk-preferring rats trained on tasks that don’t feature win-paired cues still exhibit flexibility in choice. We have added the following point to the discussion to address this:

“While risk-preferring rats exhibit some degree of distortion in reward valuation, as they do not follow the most rewarding strategy (i.e., selecting optimal options), we believe this to be at least partially separable from choice inflexibility, as risk-preferring rats on tasks that don’t feature win-paired cues remain sensitive to devaluation.”

While the overall computational approach is excellent, I believe that the choice of computational models is poor. Loss trials come at a double cost, something the authors might want to elaborate more upon, firstly the lost opportunity of not having selected a winning option which is reflected in Q-learning by the fact that r=0, and secondly a waiting period which will affect the overall reward rate. The authors choose to combine these costs by attempting to convert the time penalty into "reward currency" using three different functions that make up the three different tested models. This is a bit of a wasted opportunity as the question when comparing models is not something like "are individuals in the paired win-cue tasks more sensitive to risk? or less sensitive to time? etc" but "what is the best way of converting time into Q-value currency to fit the data?" Instead, the authors could have contrasted other models that explicitly track time as a separate variable (see for example "Impulsivity and risk-seeking as Bayesian inference under dopaminergic control" (Mikhael & Gershman 2021)) or give actions an extra risk bonus (as in "Nicotinic receptors in the VTA promote uncertainty seeking" (Naude et al 2016)).

We thank the reviewer for their thoughtful suggestions and agree that alternative modeling frameworks that explicitly track time or incorporate uncertainty bonuses would be highly informative for understanding the mechanisms underlying risky choice. However, the models employed here are drawn from previous work that required >100 rats per group for model development and validation. Due to the high degree of variability in decision making within the groups and the relatively small number of rats, this dataset is not well suited for substantial model innovation. Indeed, the most complex model from previous work had to be simplified to achieve model convergence. Testing models that greatly diverge from the previously validated RL models would make it difficult to determine whether poor model fit reflects a misspecified model or insufficient data.

We’d also like to note that the driving question for this study is to investigate the impact of different cue variants on choice patterns – untangling the relationship between timing, uncertainty, and risky choice is an important and interesting question, but beyond the scope of the present work. 

To address this limitation, we have expanded our justification of model choice in the results section to emphasize that we are applying previously developed models, with minor extensions:

“We investigated differences in the acquisition of each task variant by fitting several reinforcement learning (RL) models to early sessions. Our modeling approach closely follows methods outlined in Langdon et al. (2019), in which a much larger dataset (>100 rats per task) was used to develop the RL models applied here. Due to the comparatively small n per group in the current study, we limited our model selection to those previously validated in Langdon et al. (2019), with minor extensions.”

Another weakness of the computational section is the fact, that despite simulations having been made, figure 5 only shows the simulated risk scores and not the different choice probabilities which would be a much more interesting metric by which to judge model validity. 

We have expanded Figure 5 to show the simulated choice of each option.

In the last section, the authors ask whether the parameter estimates (obtained from optimisation on the early sessions) could be used to predict risk preference. While this is an interesting question to address, the authors give very little explanation as to how they establish any predictive relationship. A figure and more detailed explanation would have been warranted to support their claims.

We have expanded this section to provide clearer detail on the methods used to conduct this analysis and added a figure. To address a point raised by another reviewer, the statistical approach has been revised to more closely align with that used in Langdon et al. (2019), and the results have been updated appropriately:

“We next tested whether any of the subject-level parameter estimates in the nonlinear or scaled + offset model could reliably predict risk preference scores at the end of training. In Langdon et al. (2019), analyses were conducted to test whether parameters controlling sensitivity to punishment predicted final decision score at the end of training in the uncued and standard cued task variants. These analyses showed that across both task variants, there was evidence of reduced punishment sensitivity (i.e., lower m parameter or punishment learning rate) in risky versus optimal rats. We conducted similar analyses here to examine whether parameter estimates covary with decision score at end of training. To accomplish this, we fit simple linear regression models for each parameter and assessed whether the slopes were significantly different from zero.”

Why were the simulated risk scores calculated for sessions 18-20 and not 35-39 as in the experimental data, and why were the models optimised only on the first sessions?

These points were addressed in response to reviewer #1:

Based on our experience, choice patterns are well instantiated by session 20, and training only continues to 30+ sessions to achieve stability in other task variables (e.g., latencies, premature responding, etc.). That being said, the discrepancy between session numbers is confusing, so we’ve extended the simulations to match the same session numbers that were analyzed in the experimental data.

The first five sessions were chosen based on a previously developed method used in Langdon et al. (2019). When choosing the number of sessions to include, there is a balance between including more data points to improve estimation of parameters while also targeting the timeframe of maximal learning. As training continues, the impact of outcomes on subsequent choice should decrease, and the learning rate would trend towards zero. This can be observed in the reduction in inter-session choice variability as training progresses, as demonstrated in the analyses above. Once learning has ceased, presumably other cognitive processes may dictate choice (for example, habitual stimulus-response associations), which would not be appropriately captured by reinforcement learning models. It would be a separate research question to determine the point at which parameters no longer become predictive, requiring a larger dataset to thoroughly assess. We acknowledge that we did not provide sufficient justification for the learning period used for the modeling. In conjunction with the analysis of early sessions outlined above, we have added the following to the text:

“We investigated differences in the acquisition of each task variant by fitting several reinforcement learning (RL) models to early sessions. Our modeling approach closely follows methods outlined in Langdon et al. (2019), in which a much larger dataset (>100 rats per task) was used to develop the RL models applied here. Due to the comparatively small n per group in the current study, we limited our model selection to those previously validated in Langdon et al. (2019), with minor extensions. As in previous work, models were fit to valid choices from the first five sessions. As training continues, the impact of outcomes on subsequent choice should decline, and parameter values may evolve over time (e.g., decreasing learning rate). To target the period of learning during which outcomes have maximal influence over choice, and parameters likely have fixed values, we limited our analyses to the first five sessions.”

Concerning the figures, could you consider replacing or including with the bar plots, the full distribution of individual dots, or a violin plot, something to better capture the distribution of the data. This would be particularly beneficial for Figure 2B the risk score which, without a distribution suggests all individuals are optimal, something which in the text claim is not the case. 

Individual data points have been added to the relevant figures.

Is this not a case of compositional data where ANOVA is definitely not an appropriate method (compositional data consist in reporting proportions of different elements in a whole, eg this rock is 60% silicate, 20% man-made cement, etc.) because of violation of normality and mostly dependence between measurements (the sum must be 100% as in your case where knowing the proportions of P1, P2 and P3, I automatically deduce P4). I leave to you the care of finding a potential alternative. In any case, I also had difficulties understanding the varying degrees of freedom of the different reported F statistics which worry me that this has not been done properly.

This is a fair criticism, as choice proportions across P1-P4 are not fully independent. While alternative approaches do exist, there is no widely adopted or straightforward method that has been validated for this task. Accordingly, ANOVA remains the standard analytical approach for this task, as it facilitates comparison with previous work and is readily understood by readers. As mentioned in the methods, an arcsine transformation was applied to the proportional data to mitigate issues associated with bounded measures (i.e., summing to 100%). We thank the reviewer for drawing our attention to the discrepancies in the degrees of freedom – these have now been corrected.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This study provides a useful analysis of the changes in chromatin organization and gene expression that occur during the differentiation of two cell types (anterior endoderm and prechordal plate) from a common progenitor in zebrafish. Although the findings are consistent with previous work, the evidence presented in the study appears to be incomplete and would benefit from more rigorous interpretation of single-cell data, more in-depth lineage tracing, overexpression experiments with physiological levels of Ripply, and a clearer justification for using an explant system. With these modifications, this paper will be of interest to zebrafish developmental biologists investigating mechanisms underlying differentiation.

We sincerely thank the editor and the reviewers for their valuable time and efforts. Their insightful comments were greatly appreciated and have been largely addressed in the revised manuscript. We are confident that these revisions have enhanced the overall quality and clarity of our paper.

Reviewer #1 (Public review):

Summary:

During vertebrate gastrulation, mesendoderm cells are initially specified by morphogens (e.g. Nodal) and segregate into endoderm and mesoderm in part based on Nodal concentrations. Using zebrafish genetics, live imaging, and single-cell multi-omics, the manuscript by Cheng et al presents evidence to support a claim that anterior endoderm progenitors derive primarily from prechordal plate progenitors, with transcriptional regulators goosecoid (Gsc) and ripply1 playing key roles in this cell fate determination. Such a finding would represent a significant advance in our understanding of how anterior endoderm is specified in vertebrate embryos.

We would like to thank reviewer #1 for his/her comments and positive feedbacks about our manuscript.

Strengths:

Live imaging-based tracking of PP and endo reporters (Figure 2) is well executed and convincing, though a larger number of individual cell tracks will be needed. Currently, only a single cell track (n=1) is provided.

We thank the reviewer for the positive comments and the valuable suggestion. As the reviewer suggested, we re-performed live imaging analyses on the embryos of Tg(gsc:EGFP;sox17:DsRed). We tracked dozens of cells during their transformation from gsc-positive to sox17-positive. Furthermore, we performed quantification of the RFP/GFP signal intensity ratio in these cells over the course of development (Please see the revised Figure 2D and MovieS4).

Weaknesses:

(1) The central claim of the paper - that the anterior endoderm progenitors arise directly from prechordal plate progenitors - is not adequately supported by the evidence presented. This is a claim about cell lineage, which the authors are attempting to support with data from single-cell profiling and genetic manipulations in embryos and explants. The construction of gene expression (pseudo-time) trajectories, while a modern and powerful approach for hypothesis generation, should not be used as a substitute for bona fide lineage tracing methods. If the authors' central hypothesis is correct, a CRE-based lineage tracing experiment (e.g. driving CRE using a PP marker such as Gsc) should be able to label PP progenitor cells that ultimately contribute to anterior endoderm-derived tissues. Such an experiment would also allow the authors to quantify the relative contribution of PP (vs non-PP) cells to the anterior endoderm, which is not possible to estimate from the indirect data currently provided. Note: while the present version of the manuscript does describe a sox17:CRE lineage tracing experiment, this actually goes in the opposite direction that would be informative (sox:17:CRE-marked descendants will be a mixture of PP-derived and non-PP derived cells, and the Gsc-based reporter does not allow for long-term tracking the fates of these cells).

We sincerely thank the reviewer for the professional comments and the constructive suggestions. As the reviewer indicated, utilizing the single-cell transcriptomic trajectory analyses on zebrafish embryos and Nodal-injected explants system, along with the live imaging analyses on Tg(gsc:EGFP;sox17:DsRed) embryos, we revealed that anterior endoderm progenitors arise from prechordal plate progenitors. To further verify this observation, we conducted two sets of lineage-tracing assays. Initial evidence came from the results of co-injecting sox17:Cre and gsc:loxp-STOP-loxp-mcherry plasmids. We observed RFP-positive cells at 8 hpf, demonstrating the presence of cells that had expressed both genes. To explicitly follow the proposed lineage, we then implemented a reciprocal strategy, as suggested by the reviewer, that constructed and co-injected sox17:loxp-STOP-loxp-mcherry and gsc:Cre plasmids. The appearance of RFP-positive cells in the anterior dorsal region at 8 hpf provides direct evidence for a transition from gsc-positive to sox17-positive identity. These results are now included in the revised manuscript (Please see Author response image 1 and Figure S4E). However, in accordance with the reviewer's caution, we acknowledge that this does not prove this is the sole origin of anterior endoderm. Consequently, we have revised the text to clarify that our findings demonstrate that anterior endoderm can be specified from prechordal plate progenitors, without claiming that it is the only source.

Author response image 1.

Characterization of anterior endoderm lineage by Cre-Lox recombination system.

(2) The authors' descriptions of gene expression patterns in the single-cell trajectory analyses do not always match the data. For example, it is stated that goosecoid expression marks progenitor cells that exist prior to a PP vs endo fate bifurcation (e.g. lines 124-130). Yet, in Figure 1C it appears that in fact goosecoid expression largely does not precede (but actually follows) the split and is predominantly expressed in cells that have already been specified into the PP branch. Likewise, most of the cells in the endo branch (or prior) appear to never express Gsc. While these trends do indeed appear to be more muddled in the explant data (Figure 1H), it still seems quite far-fetched to claim that Gsc expression is a hallmark of endoderm-PP progenitors.

We thank the reviewer for pointing out this issue. Our initial analysis proposed that the precursors of the prechordal plate (PP) and anterior endoderm (endo) more closely resemble a PP cell fate, as their progenitor populations highly express PP marker genes, such as gsc. The gsc gene is widely recognized as a PP marker[1]. The reviewer pointed out that in our analysis, these precursor cells do not initially exhibit high gsc expression; rather, gsc expression gradually increases as PP fate is specified.

The reason for this observation is as follows: First, for the in vivo data, we used the URD algorithm to trace back all possible progenitor cells for both the PP and anterior endo trajectory. As mentioned in the manuscript, the PP and anterior endo are relatively distant in the trajectory tree of the zebrafish embryonic data. Consequently, this approach likely included other, confounding progenitor cells that do not express gsc (like ventral epiblast, Author response image 2). However, we further investigated the expression of gsc and sox17 along these two trajectories. The conclusion remains that gsc expression is indeed higher than sox17 in the progenitor cells common to both trajectories (Author response image 2). Combined with the live imaging analysis presented in this study, which shows that gsc expression increases progressively in the PP, this supports the notion that the progenitor cells for both PP and anterior endoderm initially bias towards a PP cell fate.

On the other hand, in our previously published work using the Nodal-injected explant system, which specifically induces anterior endo and PP, the cellular trajectory analysis also revealed that the specifications of PP and anterior endo follow very similar paths. Therefore, we proceeded to analyze the Nodal explant data. Similarly, when using URD to trace the differentiation trajectories of PP and anterior endo cells, a small number of other progenitor cells were also captured. This explains why a minority of cells do not express gsc—these are likely ventral epiblast cells (Author response image 2). However, based on the Nodal explant data, gsc is specifically highly expressed in the progenitor cells of the PP and anterior endo. Its expression remains high in the PP trajectory but gradually decreases in the endoderm trajectory (Figure 1H).

Author response image 2.

(A) The expression of ventral epiblast markers in PP and anterior Endo URD trajectory. (B) The expression of gsc, sox32 and sox17 in the progenitors of PP and anterior endo in embryos and Nodal explants.

(3) The study seems to refer to "endoderm" and "anterior endoderm" somewhat interchangeably, and this is potentially problematic. Most single-cell-based analyses appearing in the study rely on global endoderm markers (sox17, sox32) which are expressed in endodermal precursors along the entire ventrolateral margin. Some of these cells are adjacent to the prechordal plate on the dorsal side of the gastrula, but many (most in fact) are quite some distance away. The microscopy-based evidence presented in Figure 2 and elsewhere, however, focuses on a small number of sox17-expressing cells that are directly adjacent to, or intermingled with, the prechordal plate. It, therefore, seems problematic for the authors to generalize potential overlaps with the PP lineage to the entire endoderm, which includes cells in ventral locations. It would be helpful if the authors could search for additional markers that might stratify and/or mark the anterior endoderm and perform their trajectory analysis specifically on these cells.

We thank the reviewer for these comments and suggestions. We fully agree with the reviewer's point that the expression of sox32 and sox17 cannot be used to distinguish dorsal endoderm from ventral-lateral endoderm cells. However, during the gastrulation stage, all endodermal cells express sox32 and sox17, and there are currently no specific marker genes available to distinguish between them.

After gastrulation ends, the dorsal endoderm (i.e., the anterior endoderm) begins to express pharyngeal endoderm marker genes, such as pax1b. Therefore, in the analysis of embryonic data in vivo, when studying the segregation of the anterior endoderm and PP trajectory, we specifically used the pharyngeal endoderm as the subject to trace its developmental trajectory.

In the case of Nodal explants, Nodal specifically induces the fate of the dorsal mesendoderm, which includes both the PP and pharyngeal endoderm (anterior endoderm). Precisely for this reason, we consider the Nodal explant system as a highly suitable model for investigating the mechanisms underlying the cell fate separation between anterior endoderm and PP. Thus, in the Nodal explant data, we included all endodermal cells for downstream analysis.

To avoid any potential confusion for readers, we have revised the term "endoderm" in the manuscript to "anterior endoderm" as suggested by the reviewer.

(4) It is not clear that the use of the nodal explant system is allowing for rigorous assessment of endoderm specification. Why are the numbers of endoderm cells so vanishingly few in the nodal explant experiments (Figure 1H, 3H), especially when compared to the embryo itself (e.g. Figures 1C-D)? It seems difficult to perform a rigorous analysis of endoderm specification using this particular model which seems inherently more biased towards PP vs. endoderm than the embryo itself. Why not simply perform nodal pathway manipulations in embryos?

We sincerely thank the reviewer for raising this important question. In our study of the fate separation between the PP and anterior endoderm, we initially analyzed zebrafish embryonic data. However, when reconstructing the transcriptional lineage tree using URD, we observed that these two cell trajectories were positioned relatively far apart on the tree. Yet, existing studies have shown that the anterior endoderm and PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells[2-4], and they share transcriptional similarities[5]. Therefore, as the reviewer pointed out, when tracing all progenitor cells of these two trajectories using the URD algorithm, it is easy to include other cell types, such as ventral epiblast cells (Author response image 2). For this reason, we concluded that directly using embryonic data to dissect the mechanism of fate separation between PP and anterior endoderm might not yield highly accurate results.

In contrast, our group’s previous work, published in Cell Reports, demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including anterior endoderm, PP, and notochord[5]. Thus, we considered the Nodal explant system to be a highly suitable model for investigating the mechanism of fate separation between PP and anterior endoderm. Ultimately, by analyzing both in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further validated by live imaging experiments.

Regarding the reviewer’s concern about the relatively low number of endodermal cells in the Nodal explant system, we speculate that this is because the explants predominantly induce anterior endoderm. Since endodermal cells constitute only a small proportion of cells during gastrulation, and anterior endoderm represents an even smaller subset, the absolute number is naturally limited. Nevertheless, the anterior endodermal cells captured in our Nodal explants were sufficient to support our analysis of the fate separation mechanism between anterior endoderm and PP. Finally, to further strengthen the findings from scRNA-seq analyses, we subsequently performed live imaging validation experiments using both zebrafish embryos and the explant system.

(5) The authors should not claim that proximity in UMAP space is an indication of transcriptional similarity (lines 207-208), especially for well-separated clusters. This is a serious misrepresentation of the proper usage of the UMAP algorithm. The authors make a similar claim later on (lines 272-274).

We would like to extend our gratitude to the reviewer for their insightful comments. We have revised the descriptions regarding UMAP throughout the manuscript as suggested (Please see the main text in revised manuscript).

Reviewer # 1 (Recommendations For The Authors):

- Pseudotime trajectories constructed from single-cell snapshots are not true "lineage" measurements. Authors should refrain from referring to such data as lineage data (e.g. lines 99, 100, 103, 109, 112, 127, etc). Such models should be referred to as "trajectories", "hypothetical lineages", or something else.

We are grateful to the reviewer for this comment. Following their recommendation, we have revised the terminology from "transcriptional lineage tree" to "trajectory" across the entire manuscript (Please see main text in revised manuscript).

- The live imaging data presented in Figure 2 (and supplemental figures) are compelling and do seem to show that some cells can switch between PP and endo states. However, the number of cells reported is still too low to be able to ascertain whether or not this is just a rare/edge-case phenomenon. Tracks for just a single cell are reported in Figure 2C-D. This is insufficient. Tracks for many more cells should be collected and reported alongside this current sole (n=1) example. The choice of time window for these live imaging experiments should also be better explained. These live imaging experiments are being performed at or after 6hpf, but authors claim in the text that "... the segregation between PP and Endo has already occurred by 6hpf." (lines 126-127). Why not perform these live imaging experiments earlier, when the initial fate decision between PP and endo is supposedly occurring?

We sincerely appreciate the reviewer’s insightful questions and constructive feedback. In response, we have made several important revisions. First, the reviewer noted that our original manuscript tracked only a single cell and suggested increasing the number of tracked cells. Following this recommendation, we repeated the live-imaging experiments and expanded the number of tracked endodermal cells (Please see the revised Movie S4 and Figure 2D). The experimental conditions were kept identical to the previous setup, and these cells consistently exhibited a gradual transition from a gsc+ fate to a sox17+ endodermal fate. In addition, the reviewer recommended performing live imaging at an earlier time point (Movie S5). Accordingly, we conducted additional experiments initiating live imaging at around 5.7 hours and observed the onset of a sox17 expression in gsc+ cells at approximately 6 hpf, which is consistent with our single-cell transcriptomic analysis.

- The sections devoted to lengthy descriptions of GO terms (lines 131-146, 239-254) and receptor-ligand predictions (lines 170-185) are largely speculative. Consider streamlining.

Thanks for the reviewer's comment. We have streamlined the content related to the GO analysis as suggested (Please see Lines 128-132, 157-167, 221-225).

- The use of a "Nodal Activity Score" (lines 212-226) is clever but might actually be less informative than showing contributions from individual nodal target genes. The combining of counts data from 29 predicted nodal targets means that the contribution (or lack of contribution) from each gene becomes masked. The authors should include supplementary dot plots that break down the score across all 29 genes, allowing the reader to assess overall contributions and/or sub-clusters of gene co-expression patterns, if present.

Thank you very much for the reviewer's positive feedback on our use of the "Nodal Activity Score" and the valuable suggestions provided. Following the recommendation, we analyzed the expression of the 29 Nodal direct targets used in our study across the WT, ndr1 knockdown (kd), and lft1 knockout (ko) groups. We found that the known axial mesoderm genes, such as chrd, tbxta, noto, and gsc, contributed significantly to the Nodal score. The newly conducted analysis has been included in the Supplementary Information (Please see Figure S7L).

- The differential expression trends being reported for srcap (line 251) do not appear to be significant. Are details and P-values for these DEG tests reported somewhere in the manuscript?

We thank the reviewer for raising this question. Based on the reviewer's comment, we performed statistical tests (Wilcoxon test) to compare the expression of srcap in PP and Endo. Our analysis revealed that while srcap expression is slightly higher in PP than in Endo, this difference is not statistically significant. The specific p-value and fold change have been indicated in the revised figure (Please see Figure 4J and S7H). Based on this analysis, we revised our description to state that srcap expression is slightly higher in the PP compared to in the anterior endoderm.

- Following the drug experiments with the drug AU15330 (lines 254-263), authors have only reported #s of endodermal cells, which seem to have increased, which the authors suggest indicates a fate switch from PP to endo. However, the authors have not reported whether the numbers of PP cells decreased or stayed the same in these embryos. This would be helpful information to include, as it is very difficult to discern quantitative trends from the images presented in Fig 4H and 4L.

Thank the reviewer for his/her comments and suggestions. Following the reviewer's suggestions, we performed Imaris analysis on the HCR staining results from the DMSO (control), 1μM AU15330-treated, and 5μM AU15330-treated groups. Our analysis focused on the number of frzb-positive cells (PP), and the comparison revealed that treatment with AU15330 significantly reduces the PP cell number. These findings have been incorporated into the revised manuscript and supplementary information (Please see Figures S7J and S7K).

Reviewer #2 (Public review):

Summary:

During vertebrate gastrulation, the mesoderm and endoderm arise from a common population of precursor cells and are specified by similar signaling events, raising questions as to how these two germ layers are distinguished. Here, Cheng and colleagues use zebrafish gastrulation as a model for mesoderm and endoderm segregation. By reanalyzing published single-cell sequencing data, they identify a common progenitor population for the anterior endoderm and the mesodermal prechordal plate (PP). They find that expression levels of PP genes Gsc and ripply are among the earliest differences between these populations and that their increased expression suppresses the expression of endoderm markers. Further analysis of chromatin accessibility and Ripply cut-and-tag is consistent with direct repression of endoderm by this PP marker. This study demonstrates the roles of Gsc and Ripply in suppressing anterior endoderm fate, but this role for Gsc was already known and the effect of Ripply is limited to a small population of anterior endoderm. The manuscript also focuses extensively on the function of Nodal in specifying and patterning the mesoderm and endoderm, a role that is already well known and to which the current analysis adds little new insight.

We would like to thank the reviewer #2 for the constructive comments and positive feedback regarding our manuscript.

Strengths:

Integrated single-cell ATAC- and RNA-seq convincingly demonstrate changes in chromatin accessibility that may underlie the segregation of mesoderm and endoderm lineages, including Gsc and ripply. Identification of Ripply-occupied genomic regions augments this analysis. The genetic mutants for both genes provide strong evidence for their function in anterior mesendoderm development, although these phenotypes are subtle.

We thank the reviewer for recognizing our work, and we greatly appreciate the constructive suggestions from the reviewer.

Weaknesses:

The use of zebrafish embryonic explants for cell fate trajectory analysis (rather than intact embryos) is not justified. In both transcriptomic comparisons between the two fate trajectories of interest and Ripply cut-and-tag analysis, the authors rely too heavily on gene ontology which adds little to our functional understanding. Much of the work is focused on the role of Nodal in the mesoderm/endoderm fate decision, but the results largely confirm previous studies and again provide few new insights. Some experiments were designed to test the relationship between the mesoderm and endoderm lineages and the role of epigenetic regulators therein, but these experiments were not properly controlled and therefore difficult to interpret.

We sincerely thank the reviewer for the comments. As we previously answered, in our study of the fate differentiation between the PP and the anterior endoderm, we initially analyzed zebrafish embryonic data. However, when we used URD to reconstruct the transcriptional trajectory tree, we found that these two cell trajectories were distantly located on the tree. Existing studies have shown that the anterior endoderm and the PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells and share transcriptional similarities[2-4]. Therefore, when tracing all progenitor cells of these two trajectories using the URD algorithm, it is easy to include other cell types, such as ventral mesendodermal cells (Please see Author response image 2A). Based on this, we believe that directly using embryonic data to decipher the mechanism of fate differentiation between the PP and the anterior endoderm may not yield sufficiently precise results. In contrast, our group’s previous study published in Cell Reports demonstrated that the Nodal-induced explant system can specifically enrich dorsal mesendodermal cells, including the anterior endoderm, PP, and notochord[5]. Thus, we consider the Nodal explant system as an ideal model for studying the fate differentiation mechanism between the PP and the anterior endoderm. Ultimately, through comprehensive analysis of in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further validated by live imaging experiments.

Regarding the GO analysis, we have streamlined it as suggested by the reviewers. In the revised manuscript, we analyzed the expression of specific genes contributing to key GO functions. Additionally, in the revised version, we conducted more live imaging experiments and quantitative cell assays. We designed gRNA for srcap using the CRISPR CAS13 system to knock down srcap, which further corroborated the morpholino knockdown results, showing consistency with the morpholino data. We also performed Western blot validation of the SWI/SNF complex's response to the drug AU15330, confirming the drug's effectiveness. We hope these additional experiments adequately address the reviewers' concerns.

Reviewer #2 (Recommendations For The Authors):

(1) In the introduction, the authors state that mesendoderm segregates into mesoderm and endoderm in a Nodal-concentration dependent manner. While it is true that higher Nodal signaling levels are required for endoderm specification, A) this is also true for some mesoderm populations, and B) Work from Caroline Hill's lab has shown that Nodal activity alone is not determinative of endoderm fate. Although the authors cite this work, it is conclusions are not reflected in this over-simplified explanation of mesendoderm development. The authors also state that it is not clear when PP and endoderm can be distinguished transcriptionally, but this was also addressed in Economou et al, 2022, which found that they can be distinguished at 60% epiboly but not 50% epiboly.

We sincerely thank the reviewer for raising this question and reminding us of the conclusions drawn from that excellent study. As the reviewer pointed out, Economou et al. demonstrated that Nodal signaling alone is insufficient to determine the cell fate segregation of mesendoderm[6]. However, their study primarily focused on the fate segregation of the ventral-lateral mesendoderm lineage. In contrast, we believe that the mechanisms underlying dorsal mesendoderm specification may differ.

First, it is well-studied that in zebrafish embryos, the most dorsal mesendoderm is initially specified by the activity of the dorsal organizer. Notably, the Nodal signaling ligands ndr1 and ndr2 begin to be expressed in the dorsal organizer as early as the sphere stage[7]. In our study, through single-cell transcriptomic trajectory analysis and live imaging analysis, we observed that the cell fate segregation of the dorsal mesendoderm can be traced back to the shield stage.

Second, the regulatory mechanisms governing dorsal mesendoderm fate differentiation may differ from those of the ventral-lateral mesendoderm. For instance, the gsc gene is exclusively expressed in the dorsal mesendoderm and is absent in the ventral-lateral mesendoderm. Given that gsc is a critical master gene, its overexpression in the ventral side can induce a complete secondary body axis. Similarly, ripply1, identified in our study, is also expressed early and specifically in the dorsal mesendoderm. Overexpression of ripply1 in the ventral side similarly induces a secondary body axis, albeit with the absence of the forebrain[5]. In this study, we found that gsc and ripply1 as the repressor, collectively inhibited dorsal (anterior) endoderm specified from PP progenitors.

In summary, our study focuses on the regulatory mechanisms of fate segregation in the dorsal (anterior) mesendoderm, which differs from the mechanisms of ventral-lateral mesendoderm lineage segregation reported by Economou et al. We believe that this distinction represents a key novelty of our work.

(2) As noted in the manuscript, Warga and Nusslein-Volhard determined long ago that PP and anterior endoderm share a common precursor. It is surprising that this close relationship is not apparent from the lineage trees in whole embryos but is apparent in lineage trees from explants. The authors speculate that the resolution of the whole embryo dataset is insufficient to detect this branch point and propose explants as the solution, but it is not clear why the explant dataset is higher resolution and/or more appropriate to address this question.

We sincerely thank the reviewer for their thoughtful comments. As we mentioned previously, our investigation of fate differentiation between the PP and the anterior endoderm initially involved the analysis of zebrafish embryonic data. However, when we used URD to reconstruct the transcriptional trajectory tree, we observed that these two cell trajectories were located far apart. Previous elegant studies, as the reviewer mentioned, have shown that the anterior endoderm and the PP are not only spatially adjacent but also both originate from mesendodermal progenitor cells and share transcriptional similarities[2,3,8]. Consequently, when tracing all progenitor cells of these two trajectories using the URD algorithm, other cell types—such as ventral mesendodermal cells—are easily included. Based on this, we believe that directly using embryonic data to elucidate the mechanism of fate differentiation between the PP and the anterior endoderm may lack sufficient precision.

In contrast, our group’s previous study published in Cell Reports demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including the anterior endoderm, PP, and notochord[5]. Therefore, we consider the Nodal explant system as an ideal model for studying the mechanism underlying fate differentiation between the PP and the anterior endoderm. Through comprehensive analyses of both in vivo embryonic and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitor cells—a conclusion further supported by live imaging experiments.

(3) Much of the analysis of DEGs between the lineages of interest is focused on GO term enrichment. But this logic is circular. The endoderm lineage is defined as such because it expresses endoderm-enriched genes, therefore the finding that the endoderm lineage is enriched for endoderm-related GO terms adds no new insights.

We thank the reviewer for these comments. As the reviewers suggested, in the revised manuscript, we indicated specific genes associated with key GO terms (Please see Figure 4B). Additionally, we have streamlined the content related to the GO analysis as suggested.

(4) The authors describe the experiment in Figure S4 as key evidence that Gsc+ cells can give rise to endoderm, but no controls are presented. Only a few cells are shown that express mCherry upon injection of sox17:cre constructs. Is mCherry also expressed in the occasional cell injected with Gsc:lox-stop-lox-mCherry in the absence of cre? Although they report 3 independent replicates, it appears that only 2 individual embryos express mCherry. This very small number is not convincing, especially in the absence of appropriate controls.

We thank the reviewer for raising this question. Following the reviewer's suggestion, we injected gsc:loxp-stop-loxp-mCherry into zebrafish embryos at the 1-cell stage as a control. After performing at least three independent replicates and analyzing no fewer than 100 embryos, we did not observe any mCherry-positive cells. Additionally, we co-injected gsc:loxp-stop-loxp-mCherry with sox17:cre and increased the sample size. Furthermore, we constructed plasmids of sox17:loxp-stop-loxp-mCherry and gsc:cre, and upon injection at the 1-cell stage, we observed RFP-positive cells at 8 hpf (Please see Author response image 1 and Figure S4E). Together with our live imaging data, these experiments collectively demonstrate that anterior endodermal cells can originate from PP progenitors.

(5) The authors spend a lot of effort demonstrating that PP and anterior endoderm are Nodal dependent. First, these data (especially Figures 3E and 3I) are not very convincing, as the differences shown are very small or not apparent. Second, this is already well-known and adds nothing to our understanding of mesoderm-endoderm segregation.

We sincerely thank the reviewer for their insightful questions. First, the reviewer mentioned that in the initial version of our manuscript, the effects of ndr1 knockdown and lefty1 knockout on Nodal signaling and cell fate—particularly prechordal plate (PP) and anterior endoderm (endo)—in Nodal-induced explants were not very pronounced. We recognize that the negative feedback mechanism between Nodal and Lefty signaling may explain why Nodal acts as a morphogen, regulating pattern formation through a Turing-like model[9]. Therefore, knocking down a Nodal ligand gene, such as ndr1 in this study, or knocking out a Nodal inhibitor, such as lft1, may only have a subtle impact on Nodal signaling[10].

Accordingly, in this study, we performed extensive pSmad2 immunofluorescence analysis and observed that although the overall intensity of Nodal activity did not change dramatically, there was a statistically significant difference. Importantly, this subtle variation in Nodal signaling strength is precisely what we intended to capture, since PP and anterior endoderm are highly sensitive to Nodal signaling[11], and even minor differences may bias their fate segregation.

This leads directly to the reviewer’s second concern. While numerous studies suggest that the strength of Nodal signaling influences mesendodermal fate—with high Nodal promoting endoderm and lower concentrations inducing mesoderm—most of these studies focus on ventral-lateral mesendoderm development[4,6,10]. In contrast, the mechanisms underlying dorsal mesendoderm fate specification differ, which is a key innovation of our study.

Previous work by Bernard Thisse and colleagues demonstrated that even a slight reduction in Nodal signaling, achieved by overexpressing a Nodal inhibitor, is sufficient to cause defects in the specification of PP and endoderm[11]. This indicates that PP and endoderm require the highest levels of Nodal signaling for proper specification. Moreover, the most dorsal mesendoderm, PP and anterior endoderm are not only spatially adjacent but also share similar transcriptional states, making the regulation of their fate separation particularly challenging to study.

The Dr. C.P. lab made important contributions to this issue, showing that the duration of Nodal exposure is critical for segregating PP and anterior endoderm fates: prolonged Nodal signaling promotes expression of the transcriptional repressor Gsc, which directly suppresses the key endodermal transcription factor Sox17, thereby inhibiting anterior endoderm specification[3]. They also found that tight junctions among PP cells facilitate Nodal signal propagation[8]. However, their studies revealed that Gsc mutants do not exhibit endodermal phenotypes, suggesting that additional factors or mechanisms regulate PP versus anterior endoderm fate separation[3].

In our study, we first observed that subtle differences in Nodal concentration may bias the fate choice between PP and anterior endoderm. Given that ndr1 knockdown and lft1 knockout mildly reduce or enhance Nodal signaling, respectively, we reasoned that using these two perturbations in a Nodal-induced explant system combined with single-cell RNA sequencing could generate transcriptomic profiles under slightly reduced and enhanced Nodal signaling. This approach may help identify key decision points and transcriptional differences during PP and anterior endoderm segregation, ultimately uncovering the molecular mechanisms downstream of Nodal that govern their fate separation.

(6) The authors claim that scrap expression differs between the 2 lineages of interest, but this is not apparent from Figure 4J-K. Experiments testing the role of SWI/SNF and scrap also require additional controls. Can scrap MO phenotypes be rescued by scrap RNA? Is there validation that SWI/SNF components are degraded upon treatment with AU15330?

We are very grateful for the reviewers' questions. Using single-cell data from zebrafish embryos and Nodal explants, we compared the expression of srcap in the PP and anterior Endo cell populations. We found that srcap expression showed a slight increase in PP compared to anterior Endo, but the difference was not statistically significant (Please see Figure 4J and S7H). Therefore, we modified our description in the revised manuscript. However, we speculate that this slight difference might influence the distinct cell fate specification between PP and anterior endo. In the original version of the manuscript, we reported that either treatment with AU15330, an inhibitor of the SWI/SNF complex, or injection of morpholino targeting srcap—a key component of the SWI/SNF complex—enhanced anterior endo fate while reducing PP cell specification. During this round of revision, we initially attempted to follow the reviewer’s suggestion to co-inject srcap mRNA along with srcap morpholino to rescue the phenotype. However, we found that the length of srcap mRNA exceeds 10,000 bp, and despite multiple attempts, we were unable to successfully obtain the srcap mRNA. Therefore, we were unable to perform the rescue experiment and instead adopted an alternative approach to validate the function of srcap. We aimed to use anthor knockdown approach (CRISPR/Cas system) to determine whether a phenotype similar to that observed with morpholino knockdown could be achieved. Using the CRISPR/Cas13 system, we designed gRNA targeting srcap, knocked down srcap, and examined the cell specification of PP and anterior endo. We found that, consistent with our previous results, knocking down srcap obviously reduced PP cell fate while increasing anterior endo cell fate (Author response image 3). Additionally, the reviewer raised the question of whether the SWI/SNF complex is degraded after AU15330 treatment. Following the reviewer’s suggestion, we attempted to perform Western blot analysis on BRG1, one of the components of the SWI/SNF complex. However, despite multiple attempts, we were unable to achieve successful detection of the BRG1 protein by the antibody in zebrafish. Several studies have reported that knockdown or knockout of brg1 leads to defects in neural crest cell specification in zebrafish[12,13]. Therefore, alternatively, we treated zebrafish embryos at the one-cell stage with 0 μM (DMSO), 1 μM, and 5 μM AU15330, and examined the expression of sox10 and pigment development around 48 h. We found that treatment with 1 μM AU15330 reduced sox10 expression and pigment production, though not significantly, whereas treatment with 5 μM AU15330 significantly disrupted neural crest cell development. Thus, this experiment demonstrates that AU15330 is functional in zebrafish. (Author response image 3).

Author response image 3.

(A) Characterization of anterior endoderm and PP cells following CRISPR-Cas13d-mediated srcap knockdown. (B) Validation of srcap mRNA expression by RT‑qPCR following CRISPR‑Cas13d knockdown. (C) RT‑qPCR shows the expression of sox10 after treatment with increasing concentrations of AU15300. (D) Morphology of zebrafish embryos at 48 hpf after treatment with increasing concentrations of AU15300.

(7) The authors conclude from their chromatin accessibility analysis that variations in Nodal signaling are responsible for expression levels of PP and endoderm genes, but they do not consider the alternative explanation that FGF signaling is playing this role. Such a function for FGF was established by Caroline Hill's lab, and the authors also show in Figure S5G that FGF signaling in enriched between these cell populations.

Thank you very much for raising this issue. As the reviewer pointed out, Caroline Hill's lab has conducted elegant work demonstrating that FGF signaling plays a crucial role in the separation of ventral-lateral mesendoderm cell fates[4,6]. In contrast, our study primarily focuses on studying the mechanisms underlying the separation of dorsal mesendoderm cell fates. However, our research also reveals that FGF signaling significantly regulates the fate separation of the dorsal mesendoderm, as inhibiting FGF signaling suppresses PP cell specification while promoting anterior Endo fate. In our previously published work, we found that Nodal signaling can directly activate the expression of FGF ligand genes[5]. Therefore, we hypothesize that Nodal signaling, acting as a master regulator, activates various downstream target genes—including FGF—and how FGF signaling regulates the cell fate separation of the dorsal mesendoderm warrants further investigation in our further studies.

(8) When interpreting the results of their Ripply cut-and-run experiment, the authors again rely heavily on GO term analysis and claim that this supports a role for Ripply as a transcriptional repressor. GO term enrichment does not equal functional analysis. It would be more convincing to intersect DEGs between WT and ripply-/- embryos with Ripply-enriched loci.

Thanks for raising this important issue and the constructive suggestion. In response to the reviewer's valid concern regarding the GO term analyses from our CUT&Tag data, we implemented a more stringent filtering strategy. We identified peaks enriched in the treatment group and applied differential analysis, selecting genes with a log₂FoldChange > 3, padj < 0.05, and baseMean > 30 as high-confidence Ripply1 binding targets. A GO enrichment analysis of these genes revealed significant terms related to muscle development, consistent with Ripply1's established role in somite development, thereby validating our approach. We supplemented the related gene list in the revised manuscript. Moreover, within this refined analysis, we found that sox32 met our binding threshold, while sox17 did not. Furthermore, as suggested, we examined mespbb—a known Ripply1-repressed gene—which was present, and gsc, a Nodal target used as a negative control, which was absent. This confirms the specificity of our analysis (Figure 6 and Figure S11). Consequently, our revised analyses support a model in which Ripply1 directly binds the sox32 promoter. Given that Sox32 is a known upstream regulator of sox17, this binding provides a plausible direct mechanism for the observed regulation of sox17 expression. We have updated the figures and text accordingly. We attempted to generate ripply1^-/- mutants but found that homozygous loss results in embryonic lethality.

(9) The way N's are reported is unconventional. N= number of embryos used in the experiment, n= number of embryos imaged. If an embryo was not imaged or analyzed in any way, it cannot be considered among the embryos in an experiment. If only 4 embryos were imaged, the N for that experiment is 4 regardless of how many embryos were stained. Authors should also report not only the number of embryos examined but also the number of independent trials performed for all experiments.

Thank you very much for the reviewer's suggestion. As suggested, we have revised the description regarding the number of embryos and experimental replicates in the figure legends.

(10) The authors should avoid the use of red-green color schemes in figures to ensure accessibility for color-blind readers.

Thanks for the suggestions. We have updated the figures in our revised manuscript and adjusted the color schemes to avoid red-green combinations.

Reviewer #3 (Public Review):

Summary:

Cheng, Liu, Dong, et al. demonstrate that anterior endoderm cells can arise from prechordal plate progenitors, which is suggested by pseudo time reanalysis of published scRNAseq data, pseudo time analysis of new scRNAseq data generated from Nodal-stimulated explants, live imaging from sox17:DsRed and Gsc:eGFP transgenics, fluorescent in situ hybridization, and a Cre/Lox system. Early fate mapping studies already suggested that progenitors at the dorsal margin give rise to both of these cell types (Warga) and live imaging from the Heisenberg lab (Sako 2016, Barone 2017) also pretty convincingly showed this. However, the data presented for this point are very nice, and the additional experiments in this manuscript, however, further cement this result. Though better demonstrated by previous work (Alexander 1999, Gritsman 1999, Gritsman 2000, Sako 2016, Rogers 2017, others), the manuscript suggests that high Nodal signaling is required for both cell types, and shows preliminary data that suggests that FGF signaling may also be important in their segregation. The manuscript also presents new single-cell RNAseq data from Nodal-stimulated explants with increased (lft1 KO) or decreased (ndr1 KD) Nodal signaling and multi-omic ATAC+scRNAseq data from wild-type 6 hpf embryos but draws relatively few conclusions from these data. Lastly, the manuscript presents data that SWI/SNF remodelers and Ripply1 may be involved in the anterior endoderm - prechordal plate decision, but these data are less convincing. The SWI/SNF remodeler experiments are unconvincing because the demonstration that these factors are differentially expressed or active between the two cell types is weak. The Ripply1 gain-of-function experiments are unconvincing because they are based on incredibly high overexpression of ripply1 (500 pg or 1000 pg) that generates a phenotype that is not in line with previously demonstrated overexpression studies (with phenotypes from 10-20x lower expression). Similarly, the cut-and-tag data seems low quality and like it doesn't support direct binding of ripply1 to these loci.

In the end, this study provides new details that are likely important in the cell fate decision between the prechordal plate and anterior endoderm; however, it is unclear how Nodal signaling, FGF signaling, and elements of the gene regulatory network (including Gsc, possibly ripply1, and other factors) interact to make the decision. I suggest that this manuscript is of most interest to Nodal signaling or zebrafish germ layer patterning afficionados. While it provides new datasets and observations, it does not weave these into a convincing story to provide a major advance in our understanding of the specification of these cell types.

We sincerely thank the reviewer for their thorough and thoughtful assessment of our work. The reviewer acknowledged several strengths of our study, such as the use of multiple technical approaches to demonstrate that anterior endoderm differentiates from PP progenitor cells, and recognized the value of the newly added single-cell omics data. The reviewer also raised some concerns regarding the initial version of our work, including the SWI/SNF remodeler experiments and the Ripply1 gain-of-function experiment. In the revised manuscript, we have supplemented these parts with additional control experiments to better support our conclusions. We hope that our updated manuscript adequately addresses the points raised by the reviewer.

Major issues:

(1) UMAPs: There are several instances in the manuscript where UMAPs are used incorrectly as support for statements about how transcriptionally similar two populations are. UMAP is a stochastic, non-linear projection for visualization - distances in UMAP cannot be used to determine how transcriptionally similar or dissimilar two groups are. In order to make conclusions about how transcriptionally similar two populations are requires performing calculations either in the gene expression space, or in a linear dimensional reduction space (e.g. PCA, keeping in mind that this will only consider the subset of genes used as input into the PCA). Please correct or remove these instances, which include (but are not limited to):

p.4 107-110

p.4 112

p.8 207-208

p.10 273-275

We would like to thank the reviewer for raising this question. The descriptions of UMAP have been revised throughout the manuscript in accordance with the reviewer's suggestion (Please see the main text in the revised manuscript).

(2) Nodal and lefty manipulations: The section "Nodal-Lefty regulatory loop is needed for PP and anterior Endo fate specification" and Figure 3 do not draw any significant conclusions. This section presents a LIANA analysis to determine the signals that might be important between prechordal plate and endoderm, but despite the fact that it suggests that BMP, Nodal, FGF, and Wnt signaling might be important, the manuscript just concludes that Nodal signaling is important. Perhaps this is because the conclusion that Nodal signaling is required for the specification of these cell types has been demonstrated in zebrafish in several other studies with more convincing experiments (Alexander 1999, Gritsman 1999, Gritsman 2000, Rogers 2017, Sako 2016). While FGF has recently been demonstrated to be a key player in the stochastic decision to adopt endodermal fate in lateral endoderm (Economou 2022), the idea that FGF signaling may be a key player in the differentiation of these two cell types has strangely been relegated to the discussion and supplement. Lastly, the manuscript does not make clear the advantage of performing experiments to explore the PP-Endo decision in Nodal-stimulated explants compared to data from intact embryos. What would be learned from this and not from an embryo? Since Nodal signaling stimulates the expression of Wnts and FGFs, these data do not test Nodal signaling independent of the other pathways. It is unclear why this artificial system that has some disadvantages is used since the manuscript does not make clear any advantages that it might have had.

We sincerely thank the reviewers for their valuable comments. As mentioned in our manuscript, although a substantial number of studies have reported on the mechanisms governing the segregation of mesendoderm fate in zebrafish embryos—including the Dr. Hill laboratory’s work cited by the reviewers, which demonstrated the involvement of FGF signaling in the ventral mesendoderm fate specification—research on the regulatory mechanisms underlying anterior mesendoderm differentiation remains relatively limited. This is largely due to the challenges posed by the close physical proximity and similar transcriptional states of anterior mesendoderm cells, as well as their shared dependence on high levels of Nodal signaling for specification.

Several studies from the Dr. C.P. Heisenberg’s laboratory have attempted to elucidate the fate segregation between anterior mesendoderm cells, namely the prechordal plate (PP) and anterior endoderm (endo) cells. They found that PP cells are tightly connected, facilitating the propagation of Nodal signaling[8]. Prolonged exposure to Nodal activates the expression of Gsc, which acts as a transcriptional repressor to inhibit sox17 expression, thereby suppressing endodermal fate[3]. However, they also noted that Gsc mutants do not exhibit endoderm developmental defects, suggesting the involvement of additional factors in this process.

The reviewer inquired about our rationale for using the Nodal-injected explant system. In our investigation of the fate separation between the PP and the anterior endo, we initially analyzed zebrafish embryonic data. Using URD to reconstruct the transcriptional lineage tree, we found that these two cell types were positioned distantly from each other. However, existing literature indicates that the anterior endoderm and PP are not only spatially adjacent but also derive from common mesendodermal progenitors and exhibit transcriptional similarities[2,8]. As the reviewer noted, when tracing all progenitor cells of these two lineages using URD, it is easy to inadvertently include other cell types—such as ventral epiblast cells—which may compromise the accuracy of the analysis. We therefore concluded that directly using embryonic data to dissect the mechanism of fate separation between PP and anterior endoderm might not yield highly precise results.

By contrast, our group’s earlier study published in Cell Reports demonstrated that the Nodal-induced explant system specifically enriches dorsal mesendodermal cells, including anterior endo, PP, and notochord[5]. This makes the Nodal explant system a highly suitable model for studying the fate separation between PP and anterior endo. Ultimately, by analysing in vivo embryonic data and Nodal explant data, we consistently found that the anterior endoderm likely originates from PP progenitors—a conclusion further supported by live imaging experiments.

As we answered above, we first used the analyses of single-cell RNA sequencing and live imaging to demonstrate that anterior endoderm can originate from PP progenitor cells. Understanding the mechanism underlying the fate segregation between these two cell populations became a key focus of our research. We began by applying cell communication analysis to our single-cell data to identify signaling pathways that may be involved. This analysis specifically highlighted the Nodal-Lefty signaling pathway. Since Lefty acts as an inhibitor of Nodal signaling, we hypothesized that differences in Nodal signaling strength might regulate the fate of these two cell populations. By overexpressing different concentrations of Nodal mRNA and examining the fates of PP and anterior Endo cells, we confirmed this hypothesis.

Thus, we propose that even subtle differences in Nodal signaling levels may influence anterior mesendoderm fate decisions. To test this, we generated systems with slightly reduced Nodal signaling (via ndr1 knockdown) and slightly elevated Nodal signaling (via lft1 knockout). Using these models, we precisely captured the critical stage of fate segregation between PP and anterior endo cells and identified a novel transcriptional repressor, Ripply1, which works in concert with Gsc to suppress anterior endoderm differentiation.

(3) ripply1 mRNA injection phenotype inconsistent with previous literature: The phenotype presented in this manuscript from overexpressing ripply1 mRNA (Fig S11) is inconsistent with previous observations. This study shows a much more dramatic phenotype, suggesting that the overexpression may be to a non-physiological level that makes it difficult to interpret the gain-of-function experiments. For instance, Kawamura et al 2005 perform this experiment but do not trigger loss of head and eye structures or loss of tail structures. Similarly, Kawamura et al 2008 repeat the experiment, triggering a mildly more dramatic shortening of the tail and complete removal of the notochord, but again no disturbance of head structures as displayed here. These previous studies injected 25 - 100 pg of ripply1 mRNA with dramatic phenotypes, whereas this study uses 500 - 1000 pg. The phenotype is so much more dramatic than previously presented that it suggests that the level of ripply1 overexpression is sufficiently high that it may no longer be regulating only its endogenous targets, making the results drawn from ripply1 overexpression difficult to trust.

We sincerely thank the reviewer for raising this question. First, we apologize for not providing a detailed description of the amount of HA-ripply1 mRNA injected in our previous manuscript. We injected 500 pg of HA-ripply1 mRNA at the 1-cell stage and allowed the embryos to develop until 6 hpf for the CUT&Tag experiment. In the supplementary materials, we included a bright-field image of an 18 hpf-embryo injected with HA-ripply1 mRNA, which morphologically exhibited severe developmental abnormalities. The reviewer pointed out that the amount of ripply1 mRNA we injected might be excessive, potentially leading to non-specific gain-of-function effects. The injection dose of 500 pg was determined based on conclusions from our previous study. In that study, injecting 24 pg of ripply1 mRNA into one cell of zebrafish embryos at the 16–32 cell stage was sufficient to induce a secondary axis lacking the forebrain[5]. From this, we estimated that an injection concentration of approximately 500–1000 pg would be appropriate at the 1-cell stage, so that after several rounds of cell division, each cell gained 20-30 pg mRNA at 32 cell stage. Additionally, we conducted supplementary experiments injecting 100 pg, 250 pg, and 500 pg of ripply1 mRNA, and observed 500 pg of ripply1 mRNA led to a dramatic suppression of endoderm formation (Author response image 4).

Finally, our study focuses on the mechanism of cell fate segregation in the anterior mesendoderm, primarily during gastrulation. The embryos injected with ripply1 mRNA underwent normal gastrulation, and our CUT&Tag experiment was performed at 6 hpf. Therefore, we believe that the amount of ripply1 mRNA injected in this study is appropriate for addressing our research question.

Author response image 4.

Different concentrations of ripply1 mRNA were injected into zebrafish embryos at the one-cell stage, with RFP fluorescence labeling sox17-positive cells.

(4) Ripply1 binding to sox17 and sox32 regulatory regions not convincing: The Cut and Tag data presented in Fig 6J-K does not seem to be high quality and does not seem to provide strong support that Ripply 1 binds to the regulatory regions of these genes. The signal-to-noise ratio is very poor, and the 'binding' near sox17 that is identified seems to be even coverage over a 14 kb region, which is not consistent with site-specific recruitment of this factor, and the 'peaks' highlighted with yellow boxes do not appear to be peaks at all. To me, it seems this probably represents either: (1) overtagmentation of these samples or (2) an overexpression artifact from injection of too high concentration of ripply1-HA mRNA. In general, Cut and Tag is only recommended for histone modifications, and Cut and Run would be recommended for transcriptional regulators like these (see Epicypher's literature). Given this and the previous point about Ripply1 overexpression, I am not convinced that Ripply1 regulates endodermal genes. The existing data could be made somewhat more convincing by showing the tracks for other genes as positive and negative controls, given that Ripply1 has known muscle targets (how does its binding look at those targets in comparison) and there should be a number of Nodal target genes that Ripply1 does not bind to that could be used as negative controls. Overall this experiment doesn't seem to be of high enough quality to drive the conclusion that Ripply1 directly binds near sox17 and sox32 and from the data presented in the manuscript looks as if it failed technically.

We sincerely thank the reviewer for raising this question. We apologize that the binding regions of sox17 marked in our previous analysis were incorrect, and we have made the corresponding revisions in the latest version of the manuscript.

The reviewer noted that our CUT&Tag data contain considerable noise. To address this, we further refined our data processing: we annotated all peaks enriched in the treatment group and performed differential analysis, selecting genes with log₂FoldChange > 3, padj < 0.5, and baseMean > 30 as candidate targets of Ripply1 binding. Subsequent GO enrichment analysis of these genes revealed significant enrichment of muscle development-related GO terms, which is consistent with previously reported roles of Ripply1 in regulating somite development. Therefore, we believe our filtering method effectively removes a large number of noise peaks and their associated genes.

Under these screening criteria, we found that sox32 meets the threshold, while sox17 does not. In addition, following the reviewer’s suggestion, we examined mespbb—a known gene repressed by Ripply1—and gsc, a Nodal target gene, as a negative control.

Based on these new analyses, we have revised our figures and text accordingly. Our data now support the possibility that Ripply1 may directly bind to the promoter region of sox32. Since sox32 acts as a direct upstream regulator of sox17, this binding could influence sox17 expression (Figure 6 and Figure S11).

Finally, we would like to note that studies have reported Ripply1 as a transcriptional repressor, which may function by recruiting other co-factors, such as Groucho, to form a complex[14,15]. This might explain why our CUT&Tag data detected Ripply1 binding to a broad set of genes.

(5) "Cooperatively Gsc and ripply1 regulate": I suggest avoiding the term "cooperative," when describing the relationship between Ripply1 and Gsc regulation of PP and anterior endoderm - it evokes the concept of cooperative gene regulation, which implies that these factors interact with each biochemically in order to bind to the DNA. This is not supported by the data in this manuscript, and is especially confusing since Ripply1 is thought to require cooperative binding with a T-box family transcription factor to direct its binding to the DNA.

We sincerely thank the reviewer for raising this important issue. The reviewer pointed out that the term "Cooperatively" may not be entirely appropriate in the context of our study. In accordance with the reviewer's suggestion, we have replaced "Cooperatively" with "Collectively" in the relevant sections.

(6) SWI/SNF: The differential expression of srcap doesn't seem very remarkable. The dot plots in the supplement S7H don't help - they seem to show no expression at all in the endoderm, which is clearly a distortion of the data, since from the violin plots it's obviously expressed and the dot-size scale only ranges from ~30-38%. Please add to the figure information about fold-change and p-value for the differential expression. Publicly available scRNAseq databases show scrap is expressed throughout the entire early embryo, suggesting that it would be surprising for it to have differential activity in these two cell types and thereby contribute to their separate specification during development. It seems equally possible that this just mildly influences the level of Nodal or FGF signaling, which would create this effect.

Thank the Reviewer for this question. As suggested, we performed Wilcoxon tests to compare srcap expression between PP and Endo populations. The analysis shows that while srcap expression is moderately elevated in PP compared to in Endo, this difference is not statistically significant. The corresponding p-value and fold change have now been included in the revised figure (Please see Figure 4J and S7H). Although the transcriptional level of srcap shows no significant difference between PP and anterior endoderm, our subsequent experiments—using AU15330 (an inhibitor of the SWI/SNF complex) and injecting morpholino targeting srcap, a key component of the SWI/SNF complex—demonstrated that its inhibition indeed promotes anterior endoderm fate while reducing PP cell specification. Therefore, we propose that subtle differences in the SWI/SNF complex may regulate the fate specification of PP and anterior endoderm through two mechanisms. First, as mentioned in our study, these chromatin remodelers modulate the expression of master regulators such as Gsc and Ripply1, thereby influencing cell fate decisions. Second, as noted by the reviewer, these chromatin remodelers may affect the interpretation of Nodal signaling, ultimately contributing to the divergence between PP and anterior endoderm fates.

The multiome data seems like a valuable data set for researchers interested in this stage of zebrafish development. However, the presentation of the data doesn't make many conclusions, aside from identifying an element adjacent to ripply1 whose chromatin is open in prechordal plate cells and not endodermal cells and showing that there are a number of loci with differential accessibility between these cell types. That seems fairly expected since both cell types have several differentially expressed transcriptional regulators (for instance, ripply1 has previously been demonstrated in multiple studies to be specific to the prechordal plate during blastula stages). The manuscript implies that SWI/SNF remodeling by Srcap is responsible for the chromatin accessibility differences between these cell types, but that has not actually been tested. It seems more likely that the differences in chromatin accessibility observed are a result of transcription factors binding downstream of Nodal signaling.

We thank the reviewer for recognizing the value of our newly generated data. Through integrative analysis of single-cell data from wild-type, ndr1 kd, and lft1 ko groups of Nodal-injected explants at 6 hours post-fertilization (hpf), we identified a critical branching point in the fate segregation of the prechordal plate (PP) and anterior endoderm (Endo), where chromatin remodelers may play a significant role. Based on this finding, we performed single-cell RNA and ATAC sequencing on zebrafish embryos at 6 hpf. Analysis of this multi-omics dataset revealed that transcriptional repressors such as Gsc, Ripply1, and Osr1 exhibit differences in both transcriptional and chromatin accessibility levels between the PP and anterior Endo. Subsequent overexpression and loss-of-function experiments further demonstrated that Gsc and Ripply1 collaboratively suppress endodermal gene expression, thereby inhibiting endodermal cell fate. Previous studies have reported that for the activation of certain Nodal downstream target genes, the pSMAD2 protein of the Nodal signaling pathway recruits chromatin remodelers to facilitate chromatin opening and promote further transcription of target genes[16]. Therefore, our data provide chromatin accessibility profiles for Gsc and Ripply1, offering a valuable resource for future investigations into their pSMAD2 binding sites.

Minor issues:

Figure 2 E-F: It's not clear which cells from E are quantitated in F. For instance, the dorsal forerunner cells are likely to behave very differently from other endodermal progenitors in this assay. It would be helpful to indicate which cells are analyzed in Fig F with an outline or other indicator of some kind. Or - if both DFCs and endodermal cells are included in F, to perhaps use different colors for their points to help indicate if their fluorescence changes differently.

Thank you for the reviewer's suggestion. In the revised version of the figure, we have outlined the regions of the analyzed cells.

Fig 3 J: Should the reference be Dubrulle et al 2015, rather than Julien et al?

Thanks, we have corrected.

References:

Alexander, J. & Stainier, D. Y. A molecular pathway leading to endoderm formation in zebrafish. Current biology : CB 9, 1147-1157 (1999).

Barone, V. et al. An Effective Feedback Loop between Cell-Cell Contact Duration and Morphogen Signaling Determines Cell Fate. Dev. Cell 43, 198-211.e12 (2017).

Economou, A. D., Guglielmi, L., East, P. & Hill, C. S. Nodal signaling establishes a competency window for stochastic cell fate switching. Dev. Cell 57, 2604-2622.e5 (2022).

Gritsman, K. et al. The EGF-CFC protein one-eyed pinhead is essential for nodal signaling. Cell 97, 121-132 (1999).

Gritsman, K., Talbot, W. S. & Schier, A. F. Nodal signaling patterns the organizer. Development (Cambridge, England) 127, 921-932 (2000).

Kawamura, A. et al. Groucho-associated transcriptional repressor ripply1 is required for proper transition from the presomitic mesoderm to somites. Developmental cell 9, 735-744 (2005).

Kawamura, A., Koshida, S. & Takada, S. Activator-to-repressor conversion of T-box transcription factors by the Ripply family of Groucho/TLE-associated mediators. Molecular and cellular biology 28, 3236-3244 (2008).

Sako, K. et al. Optogenetic Control of Nodal Signaling Reveals a Temporal Pattern of Nodal Signaling Regulating Cell Fate Specification during Gastrulation. Cell Rep. 16, 866-877 (2016).

Rogers, K. W. et al. Nodal patterning without Lefty inhibitory feedback is functional but fragile. eLife 6, e28785 (2017).

Warga, R. M. & Nüsslein-Volhard, C. Origin and development of the zebrafish endoderm. Development 126, 827-838 (1999).

References:

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(2) Warga, R.M., and Nusslein-Volhard, C. (1999). Origin and development of the zebrafish endoderm. Development (Cambridge, England) 126, 827-838. 10.1242/dev.126.4.827.

(3) Sako, K., Pradhan, S.J., Barone, V., Inglés-Prieto, Á., Müller, P., Ruprecht, V., Čapek, D., Galande, S., Janovjak, H., and Heisenberg, C.P. (2016). Optogenetic Control of Nodal Signaling Reveals a Temporal Pattern of Nodal Signaling Regulating Cell Fate Specification during Gastrulation. Cell reports 16, 866-877. 10.1016/j.celrep.2016.06.036.

(4) van Boxtel, A.L., Economou, A.D., Heliot, C., and Hill, C.S. (2018). Long-Range Signaling Activation and Local Inhibition Separate the Mesoderm and Endoderm Lineages. Developmental cell 44, 179-191.e175. 10.1016/j.devcel.2017.11.021.

(5) Cheng, T., Xing, Y.Y., Liu, C., Li, Y.F., Huang, Y., Liu, X., Zhang, Y.J., Zhao, G.Q., Dong, Y., Fu, X.X., et al. (2023). Nodal coordinates the anterior-posterior patterning of germ layers and induces head formation in zebrafish explants. Cell reports 42, 112351. 10.1016/j.celrep.2023.112351.

(6) Economou, A.D., Guglielmi, L., East, P., and Hill, C.S. (2022). Nodal signaling establishes a competency window for stochastic cell fate switching. Developmental cell 57, 2604-2622 e2605. 10.1016/j.devcel.2022.11.008.

(7) Schier, A.F., and Talbot, W.S. (2005). Molecular genetics of axis formation in zebrafish. Annual review of genetics 39, 561-613. 10.1146/annurev.genet.37.110801.143752.

(8) Barone, V., Lang, M., Krens, S.F.G., Pradhan, S.J., Shamipour, S., Sako, K., Sikora, M., Guet, C.C., and Heisenberg, C.P. (2017). An Effective Feedback Loop between Cell-Cell Contact Duration and Morphogen Signaling Determines Cell Fate. Developmental cell 43, 198-211.e112. 10.1016/j.devcel.2017.09.014.

(9) Muller, P., Rogers, K.W., Jordan, B.M., Lee, J.S., Robson, D., Ramanathan, S., and Schier, A.F. (2012). Differential diffusivity of Nodal and Lefty underlies a reaction-diffusion patterning system. Science (New York, N.Y.) 336, 721-724. 10.1126/science.1221920.

(10) Rogers, K.W., Lord, N.D., Gagnon, J.A., Pauli, A., Zimmerman, S., Aksel, D.C., Reyon, D., Tsai, S.Q., Joung, J.K., and Schier, A.F. (2017). Nodal patterning without Lefty inhibitory feedback is functional but fragile. eLife 6. 10.7554/eLife.28785.

(11) Thisse, B., Wright, C.V., and Thisse, C. (2000). Activin- and Nodal-related factors control antero-posterior patterning of the zebrafish embryo. Nature 403, 425-428. 10.1038/35000200.

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(15) Kawamura, A., Koshida, S., and Takada, S. (2008). Activator-to-repressor conversion of T-box transcription factors by the Ripply family of Groucho/TLE-associated mediators. Mol Cell Biol 28, 3236-3244. 10.1128/MCB.01754-07.

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Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aimed to elucidate the recruitment order and assembly of the Cdv proteins during Sulfolobus acidocaldarius archaeal cell division using a bottom-up reconstitution approach. They employed liposome-binding assays, EM, and fluorescence microscopy with in vitro reconstitution in dumbbellshaped liposomes to explore how CdvA, CdvB, and the homologues of ESCRT-III proteins (CdvB, CdvB1, and CdvB2) interact to form membrane remodeling complexes.

The study sought to reconstitute the Cdv machinery by first analyzing their assembly as two subcomplexes: CdvA:CdvB and CdvB1:CdvB2ΔC. The authors report that CdvA binds lipid membranes only in the presence of CdvB and localizes preferentially to membrane necks. Similarly, the findings on CdvB1:CdvB2ΔC indicate that truncation of CdvB2 facilitates filament formation and enhances curvature sensitivity in interaction with CdvB1. Finally, while the authors reconstitute a quaternary CdvA:CdvB:CdvB1:CdvB2 complex and demonstrate its enrichment at membrane necks, the mechanistic details of how these complexes drive membrane remodeling by subcomplexes removal by the proteasome and/or CdvC remain speculative.

Although the work highlights intriguing similarities with eukaryotic ESCRT-III systems and explores unique archaeal adaptations, the conclusions drawn would benefit from stronger experimental validation and a more comprehensive mechanistic framework.

Strengths:

The study of machinery assembly and its involvement in membrane remodeling, particularly using bottom-up reconstituted in vitro systems, presents significant challenges. This is particularly true for systems like the ESCRT-III complex, which localizes uniquely at the lumen of membrane necks prior to scission. The use of dumbbell-shaped liposomes in this study provides a promising experimental model to investigate ESCRT-III and ESCRT-III-like protein activity at membrane necks.

The authors present intriguing evidence regarding the sequential recruitment of ESCRT-III proteins in crenarchaea-a close relative of eukaryotes. This finding suggests that the hierarchical recruitment characteristic of eukaryotic systems may predate eukaryogenesis, which is a significant and exciting contribution. However, the broader implications of these findings for membrane remodeling mechanisms remain speculative, and the study would benefit from stronger experimental validation and expanded contextualization within the field.

We thank the Referee for his/her appreciation of our work.

Weaknesses:

This manuscript presents several methodological inconsistencies and lacks key controls to validate its claims. Additionally, there is insufficient information about the number of experimental repetitions, statistical analyses, and a broader discussion of the major findings in the context of open questions in the field.

We have now added more controls, information about repetitions, and discussion.

Reviewer #2 (Public review):

Summary:

The Crenarchaeal Cdv division system represents a reduced form of the universal and ubiquitous ESCRT membrane reverse-topology scission machinery, and therefore a prime candidate for synthetic and reconstitution studies. The work here represents a solid extension of previous work in the field, clarifying the order of recruitment of Cdv proteins to curved membranes.

Strengths:

The use of a recently developed approach to produce dumbbell-shaped liposomes (De Franceschi et al. 2022), which allowed the authors to assess recruitment of various Cdv assemblies to curved membranes or membrane necks; reconstitution of a quaternary Cdv complex at a membrane neck.

We thank the Referee for his/her appreciation of the work.

Weaknesses:

The manuscript is a bit light on quantitative detail, across the various figures, and several key controls are missing (CdvA, B alone to better interpret the co-polymerisation phenotypes and establish the true order of recruitment, for example) - addressing this would make the paper much stronger. The authors could also include in the discussion a short paragraph on implications for our understanding of ESCRT function in other contexts and/or in archaeal evolution, as well as a brief exploration of the possible reasons for the discrepancy between the foci observed in their liposome assays and the large rings observed in cells - to better serve the interests of a broad audience.

We have now added more controls, information about repetitions, and discussion.

Reviewer #3 (Public review):

Summary:

In this report, De Franceschi et al. purify components of the Cdv machinery in archaeon M. sedula and probe their interactions with membrane and with one-another in vitro using two main assays - liposome flotation and fluorescent imaging of encapsulated proteins. This has the potential to add to the field by showing how the order of protein recruitment seen in cells is related to the differential capacity of individual proteins to bind membranes when alone or when combined.

Strengths:

Using the floatation assay, they demonstrate that CdvA and CdvB bind liposomes when combined. While CdvB1 also binds liposomes under these conditions, in the floatation assay, CdvB2 lacking its C-terminus is not efficiently recruited to membranes unless CdvAB or CdvB1 are present. The authors then employ a clever liposome assay that generates chained spherical liposomes connected by thin membrane necks, which allows them to accurately control the buffer composition inside and outside of the liposome. With this, they show that all four proteins accumulate in necks of dumbbell-shaped liposomes that mimic the shape of constricting necks in cell division. Taken altogether, these data lead them to propose that Cdv proteins are sequentially recruited to the membrane as has also been suggested by in vivo studies of ESCRT-III dependent cell division in crenarchaea.

We thank the Referee for his/her appreciation of the work.

Weaknesses:

These experiments provide a good starting point for the in vitro study the interaction of Cdv system components with the membrane and their consecutive recruitment. However, several experimental controls are missing that complicate their ability to draw strong conclusions. Moreover, some results are inconsistent across the two main assays which make the findings difficult to interpret:

(1) Missing controls.

Various protein mixtures are assessed for their membrane-binding properties in different ways. However, it is difficult to interpret the effect of any specific protein combination, when the same experiment is not presented in a way that includes separate tests for all individual components. In this sense, the paper lacks important controls. For example, Fig 1C is missing the CdvB-only control. The authors remark that CdvB did not polymerise (data not shown) but do not comment on whether it binds membrane in their assays. In the introduction, Samson et al., 2011 is cited as a reference to show that CdvB does not bind membrane. However, here the authors are working with protein from a different organism in a different buffer, using a different membrane composition and a different assay. Given that so many variables are changing, it would be good to present how M. sedula CdvB behaves under these conditions.

We thank the referee for raising this point. We have now added these data in Figure 1C. Indeed it turns out that CdvB from M. sedula exhibits clear membrane binding on its own in a flotation assay.

Similarly, there is no data showing how CdvB alone or CdvA alone behave in the dumbbell liposome assay.

Without these controls, it's impossible to say whether CdvA recruits CdvB or the other way around. The manuscript would be much stronger if such data could be added.

We have now added these data in Figure 1E, 1F and 1G. Overall, we can confirm that CdvA binds the membrane better in the presence of CdvB (although both proteins can bind the membrane on their own). Both proteins appear to recognize the curved region of the membrane neck.

(2) Some of the discrepancies in the data generated using different assays are not discussed.

The authors show that CdvB2∆C binds membrane and localizes to membrane necks in the dumbbell liposome assay, but no membrane binding is detected in the flotation assay. The discrepancy between these results further highlights the need for CdvB-only and CdvA-only controls.

We have now added these controls in Figure 1. In addition, we would like to clarify that the flotation assay and the SMS dumbbell assay serve different purposes and are not directly comparable in quantitative terms. In the flotation assay, all the protein present as input is eventually recovered and visualized. Thus, quantitative information on the proportion of the fraction of the total protein bound to lipids can be inferred from this assay. The SMS assay, in contrast, provides a very different kind of information. Because of the particular protocol required to generate dumbbells (De Franceschi, 2022), the total amount of protein in the inner buffer in dumbbells is not accurately defined, because protein that is not correctly reconstituted (e.g. which aggregates while still in the droplet phase) will interfere with vesicle generation, with the result that dumbbell with such aggregates is generally not formed in the first place. This renders it impossible to draw any quantitative conclusions about the proportion of the sample bound to lipids. The SMS is therefore not directly comparable to the flotation assay, and it is rather complementary to it. Indeed, the purpose of the SMS is to provide information about curvature selectivity of the protein.

(3) Validation of the liposome assay.

The experimental setup to create dumbbell-shaped liposomes seems great and is a clever novel approach pioneered by the team. Not only can the authors manipulate liposome shape, they also state that this allows them to accurately control the species present on the inside and outside of the liposome. Interpreting the results of the liposome assay, however, depends on the geometry being correct. To make this clearer, it would seem important to include controls to prove that all the protein imaged at membrane necks lie on the inside of liposomes. In the images in SFig3 there appears to be protein outside of the liposome. It would also be helpful to present data to show test whether the necks are open, as suggested in the paper, by using FRAP or some other related technique.

We thank the Referee for his/her appreciation. The proteins are encapsulated inside the liposomes, not outside of them. While Figure S3 might give the appearance that there is some protein outside, this is actually just an imaging artifact. Author response image 1 (below) explains this: When the membrane and protein channel are shown separately, it is clear that the protein cluster that appeared to be ‘outside’ actually colocalizes with an extra small dumbbell lobe (yellow arrowhead). The protein appeared to be outside of it because (1) the protein fluorescent signal is stronger than the signal from the membrane, and (2) there is a certain time delay in the acquisition of the two channels (0.5-1 second), thus the membrane may have slightly shifted out of focus when the fluorescence was being acquired. We are confident that the protein is inside in these dumbbells because the procedure for preparing the dumbbells requires extensive emulsification by pipetting, which requires ≈ 1 minute. This time is more than sufficient for proteins with high affinity for the membrane, like ESCRT and Cdv, to bind the membrane. For an example of how fast binding under confinement can be, please see movie 2 from this paper: De Franceschi N, Alqabandi M, Miguet N, Caillat C, Mangenot S, Weissenhorn W, Bassereau P. The ESCRT protein CHMP2B acts as a diffusion barrier on reconstituted membrane necks. J Cell Sci. 2018 Aug 3;132(4):jcs217968.

Moreover, in many instances, we observed that the protein is inside because, by increasing the gain in the images post-acquisition, a clear protein signal appear in the lumen (see Author response image 2).

Author response image 1.

Separate channels showing colocalization of protein and lipids (adapted from Figure S3). The zoom-in shows separate channels, highlighting that the CdvB2 cluster that seems to be ‘outside the dumbbell’ actually colocalizes with the small terminal lobe of the dumbbell, indicating that the protein is encapsulated within that lobe.

Author response image 2.

Residual protein present inside lumen of dumbbells as visualized by increasing the brightness post-acquisition.

We are not sure what the referee means by “test whether the necks are open, as suggested in the paper”. We are confident that the lobes of dumbbells originated from a single floppy vesicle, and were therefore mutually connected with an open neck (at least at the onset of the experiment). We have performed extensive FRAP assays on dumbbells in previous papers (De Franceschi et al., ACS nano 2022 and De Franceschi et al., Nature Nanotech 2024) which unequivocally proved that these chains of dumbbells are connected with open necks. We now also performed a few FRAP assay with reconstituted Cdv proteins, which confirmed this point. We have added a movie of such an experiment to the manuscript (Movie 1).

Investigating whether the necks are open or closed after Cdv reconstitution is indeed a very relevant question, that could be rephrased as “verify whether Cdv proteins or their combination can induce membrane scission”. This is however beyond the scope of this manuscript, as the current work merely addressed the question of hierarchical recruitment of Cdv proteins at the membrane. We plan to examine this in future work.

(4) Quantification of results from the liposome assay.

The paper would be strengthened by the inclusion of more quantitative data relating to the liposome assay. Firstly, only a single field of view is shown for each condition. Because of this, the reader cannot know whether this is a representative image, or an outlier? Can the authors do some quantification of the data to demonstrate this? The line scan profiles in the supplemental figures would be an example of this, but again in these Figures only a single image is analyzed.

The images that we showed are indeed representative. The dumbbells that are generated by the SMS approach contain an “internal control”: in each dumbbell, the protein has the option of localizing at the neck or localizing elsewhere in the region of flat membrane. We see consistently that Cdv proteins have a strong preference for localizing at the neck.

We would recommend that the authors present quantitative data to show the extent of co-localization at the necks in each case. They also need a metric to report instances in which protein is not seen at the neck, e.g. CdvB2 but not CdvB1 in Fig2I, which rules out a simple curvature preference for CdvB2 as stated in line 182.

While the request for better quantitation is reasonable, this would require carrying out very significant new experiments at the microscope, which is rendered near-impossible since both first authors left the lab on to new positions.

Secondly, the authors state that they see CdvB2∆C recruited to the membrane by CdvB1 (lines 184-187, Fig 2I). However, this simple conclusion is not borne out in the data. Inspecting the CdvB2∆C panels of Fig 2I, Fig3C, and Fig3D, CdvB2∆C signal can be seen at positions which don't colocalize with other proteins. The authors also observe CdvB2∆C localizing to membrane necks by itself (Fig 2E). Therefore, while CdvB1 and CdvB2∆C colocalize in the flotation assay, there is no strong evidence for CdvB2∆C recruitment by CdvB1 in dumbbells. This is further underscored by the observation that in the presented data, all Cdv proteins always appear to localize at dumbbell necks, irrespective of what other components are present inside the liposome. Although one nice control is presented (ZipA), this suggests that more work is required to be sure that the proteins are behaving properly in this assay. For example, if membrane binding surfaces of Cdv proteins are mutated, does this lead to the accumulation of proteins in the bulk of the liposome as expected?

In the particular example of Figure 2I, it indeed appears that there are some clusters of CdvB2ΔC that do not contain CdvB1 (we indicated them in Author response image 3 by red arrowheads), while the yellow arrowheads indicate clusters that contain both proteins. It can be clearly seen that the clusters that do contain both proteins (yellow arrows) are localized at necks, while those that only contain CdvB2ΔC (red arrows) are not localized at necks. This is no coincidence. The clusters indicated by the red arrow do contain CdvB1. However, these clusters rapidly diffuse on the membrane plane because they are not fixed at the neck: therefore, they constantly shift in and out of focus. Because there is a time delay in the acquisition of each channel (between 0.5 and 1 second), these cluster were in focus when the CdvB2ΔC signal was being acquired, but sifted out of focus when the CdvB1 signal was being acquired. This implies that the clusters indicated by the yellow arrowheads are stably localized at necks, which is precisely the point we wished to make with this experiment: because Cdv proteins have an affinity for curved geometry, they preferentially and stably localize at necks. Why don’t all the clusters localize at necks then? We estimate that the simple answer is that, in this particular case, there are more clusters than there are necks, so some of the clusters must necessarily localize somewhere else.

Author response image 3.

Current Figure 2H, where clusters that are double-positive for both CdvB1 and CdvB2ΔC are indicated by yellow arrowheads, while cluster that apparently only contain CdvB2ΔC are indicated by red arrowheads. It is observed that all the double-positive clusters are localized at necks.

(5) Rings.

The authors should comment on why they never observe large Cdv rings in their experiments. In crenarchaeal cell division, CdvA and CdvB have been observed to form large rings in the middle of the 1 micron cell, before constriction. Only in the later stages of division are the ESCRTs localized to the constricting neck, at a time when CdvA is no longer present in the ring. Therefore, if the in vitro assay used by the authors really recapitulated the biology, one would expect to see large CdvAB rings in Figs 1EF. This is ignored in the model. In the proposed model of ring assembly (line 252), CdvAB ring formation is mentioned, but authors do not discuss the fact that they do not observe CdvAB rings - only foci at membrane necks. The discussion section would benefit from the authors commenting on this.

The referee is correct: it is intriguing that we don’t see micron-sized rings for CdvA and CdvB. We do note that our EM data (Fig.S1) show that CdvA in its own can form rings of about 100-200nm diameter, well below the diffraction limit, that could well correspond to the foci that we optically resolve in Figure 1. We now added a brief comment on this to the manuscript on lines 256-264.

(6) Stoichiometry

It is not clear why 100% of the visible CdvA and 100% of the the visible CdvB are shifted to the lipid fraction in 1C. Perhaps this is a matter of quantification. Can the authors comment on the stoichiometry here?

We agree that this was unclear. Since that particular gel was stained by coumassie, the quantitative signals might be unreliable, and hence we have repeated this experiment using fluorescently labelled proteins, which show indeed a less extreme distribution. This was also done to make the data more uniform, as requested by the referees.

(7) Significance of quantification of MBP-tagged filaments.

Authors use tagging and removal of MBP as a convenient, controllable system to trigger polymerisation of various Cdv proteins. However, it is unclear what is the value and significance of reporting the width and length of the short linear filaments that are formed by the MBP-tagged proteins. Presumably they are artefactual assemblies generated by the presence of the tag?

Providing a measure of the changes induced by MBP removal, in fact, validates that this actually has an effect. But perhaps this places too much emphasis on the short filaments. We now opted for a compromise, removing the quantification of the width and length of short filaments formed by MBPtagged protein from the text, but keeping the supplementary figure showing their distribution as compared to the other filaments (Figure S2E, SF).

Similar Figure 2C doesn't seem a useful addition to the paper.

We removed panel 2C, and now merely report these values in the text.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I would suggest the authors perform a deeper discussion about their findings, such as what are the evolutionary implications, how they think lipids from these archaea may affect the recruitment process,...

Because there is no exact homology between Archaea Cdv proteins and Eukaryotic ESCRT-III proteins, we do not feel our work brings new evolutionary implications beyond what we already state in the manuscript. We also dis not perform experiments using Archaea lipids, thus we would rather not speculate on how they may potentially affect the recruitment of Cdv proteins.

In general, the manuscript lacks information regarding some scale bars, number of experimental repetitions (n or N), statistical analysis when needed, information about protein concentrations used in their assays.

We have now added this information in the manuscript.

Below, I provide a list of comments that I think the authors should address to improve the manuscript:

(1) Line 113-114: The authors test protein-membrane interactions using flotation assays with positively curved SUV membranes but encapsulate proteins in dumbbell-shaped liposomes with negative curvature at the connecting necks. Might the use of membranes with opposite curvatures affect the recruitment process? Since the proteins are fluorescently labeled, I suggest testing recruitment using flat giant unilamellar vesicles or supported lipid bilayers (with zero curvature) to validate their findings.

We thank the referee for this suggestion. Please do note that we are not claiming in our paper that Cdv proteins recognize negative curvature. We merely observe that they localize at necks. The neck of a dumbbell exhibits the so-called “catenoid” geometry, which is characterized by having both positive and negative curvature.

Experimentally, on the SUVs, we now realize there was a mistake in the method section: In the flotation assay we in fact used multilamellar vesicles, not SUVs, precisely for the reason mentioned by the referee. We apologize for the oversight and have now corrected this in the methods. Multilamellar vesicles are not characterized by a strong positive curvature as SUVs do, but we do agree that they likely don’t have negative curvature there either. Because of the heterogeneous nature of the multilamellar vesicles, they provide a binding assay that was rather independent of the curvature. Complementary to the flotation assay, the SMS approach was employed to reveal the curvature preference of proteins.

Finally, we performed the experiment on large GUVs suggested by the referee using CdvB as an example, but this turned out to be inconclusive because the protein forms clusters: these clusters may be creating local curvature at the nanometer scale, which cannot be resolved by optical microscopy (Author response image 4). This is quite typical for proteins that recognize curvature (cf. for instance: De Franceschi N, Alqabandi M, Miguet N, Caillat C, Mangenot S, Weissenhorn W, Bassereau P. The ESCRT protein CHMP2B acts as a diffusion barrier on reconstituted membrane necks. J Cell Sci. 2018 Aug 3;132(4):jcs217968.)

Author response image 4.

Fluorescently labelled CdvB bound to giant unilamellar vesicle. The protein was added in the outer buffer. CdvB forms distinct clusters, which may generate a local region of high membrane curvature.

(2) Line 138-139: How is His-ZipA binding the membrane? Wouldn't Ni²⁺-NTA lipids be required? If not, how is the binding achieved?

Indeed, NTA-lipids were present. This is now stated both in the legend and in the methods.

(3) In the encapsulated protein assays, why does the luminal fluorescence intensity of the encapsulated protein sometimes appear similar to the bulk fluorescence signal? Since only a small fraction of the protein assembles at membrane necks, shouldn't the luminal pool of unbound protein show higher fluorescence intensity inside the liposomes?

We thank the referee for raising this point and giving us the opportunity to explain this. The reason is that Cdv proteins have a very high affinity for the neck, and when they cluster at the neck the fluorescence intensity of the cluster is many times higher than the background fluorescence. Because we were interested in imaging the clusters and avoiding overexposing them, we adjusted the imaging conditions accordingly, with the result that the fluorescence from both the lumen and the bulk is at very low level.

By choosing different imaging conditions, however, it can be actually seen that the signal inside the lumen is clearly higher than the bulk: this can be seen for instance in Author response image 2, where the brightness has been properly adjusted.

(4) Line 184-185: In Fig. 2I, some CdvB2ΔC puncta seem independent of CdvB1 and are not localized at membrane necks. How many such puncta exist? For example, in the provided micrograph, 2 out of 5 clusters are independent of CdvB1. This proportion is significant. Could the authors quantify the prevalence of these structures and discuss why they form?

We thank the referee for giving us the opportunity to explain this apparent discrepancy. We’ll like to stress the fact that CdvB2ΔC and CdvB1 form an obligate heterodimer: in all our experiments, without exception, we find that they form a strong complex when we mix the two proteins. This is true both in dumbbells and in flotation assays.

In the particular example of Figure 2I, it indeed appears that there are some clusters of CdvB2ΔC that do not contain CdvB1 (we indicated them in Author response image 3 by red arrowheads), while the yellow arrowheads indicate clusters that contain both proteins. It can be clearly seen that the clusters that do contain both proteins (yellow arrows) are localized at necks, while those that only contain CdvB2ΔC (red arrows) are not localized at necks. This is no coincidence. The clusters indicated by the red arrow do contain CdvB1. However, these clusters rapidly diffuse on the membrane plane because they are not fixed at the neck: therefore, they constantly shift in and out of focus. Because there is a time delay in the acquisition of each channel (between 0.5 and 1 second), these cluster were in focus when the CdvB2ΔC signal was being acquired, but sifted out of focus when the CdvB1 signal was being acquired. This implies that the clusters indicated by the yellow arrowheads are stably localized at necks, which is precisely the point we wished to make with this experiment: because Cdv proteins have affinity for curved geometry, they preferentially and stably localize at necks. Why don’t all the clusters localize at necks then?

(5) Figure 1E and 1F: Why do lipids accumulate and colocalize with the proteins? How can the authors confirm lumen connectivity between vesicles? Performing FRAP assays could validate protein localization and enrichment at the lumen of the membrane necks.

At first sight, indeed some lipid enrichment seems to be observed at the neck between lobes of dumbbells.

This is, however, an imaging artifact due to the fact that the neck is diffraction limited. As shown in the Author response image 5, we are acquiring the membrane signal from both lobes at the neck region, and therefore the signal is roughly double, hence the apparent lipid enrichment.

Author response image 5.

Schematic illustrating that the neck between two lobes is smaller than the diffraction limit of optical microscopy (the size of a typical pixel is indicated by the green square). Because of this technical limitation, the fluorescence intensity of the membrane at the neck is twice that of a single membrane.

The referee is correct in pointing out that these images do not prove that the lobes are connected, and that FRAP assays is the only way to prove this point. However, in previous papers we have confirmed extensively that in chains of dumbbells the lobes are connected:

- De Franceschi N, Pezeshkian W, Fragasso A, Bruininks BMH, Tsai S, Marrink SJ, Dekker C. Synthetic Membrane Shaper for Controlled Liposome Deformation. ACS Nano. 2022 Nov 28;17(2):966–78. doi: 10.1021/acsnano.2c06125.

- De Franceschi N, Barth R, Meindlhumer S, Fragasso A, Dekker C. Dynamin A as a one-component division machinery for synthetic cells. Nat Nanotechnol. 2024 Jan;19(1):70-76. doi: 10.1038/s41565023-01510-3.

Random sticking of liposomes would also generate clusters of vesicles, not linear chains. We now provide also a Movie (Movie 1) supporting this point.

Investigating whether the necks are open or closed after Cdv reconstitution is indeed a very relevant question, that could be rephrased as “verify whether Cdv proteins or their combination can induce membrane scission”. This is however beyond the scope of this manuscript, as the current work merely addressed the question of hierarchical recruitment of Cdv proteins at the membrane. We plan to examine this in future work.

(6) Why didn't the authors use the same lipid composition, particularly the same proportion of negatively charged lipids, on the SUVs of the flotation assays and on the dumbbell-shaped liposomes?

In flotation assays, it is typical to use a relatively large proportion of negatively charged lipids, to promote protein binding. This is because the aim is to maximize membrane coverage by the protein. The SMS procedure to generate dumbbell-shaped GUVs is completely different, however. Rather than covering the membrane with protein, the idea is to reduce the amount of protein to a minimum, so that any curvature preference can be best visualized. This is e.g. routinely done in tube pulling experiments, for the same reason (See for instance Prévost C, Zhao H, Manzi J, Lemichez E, Lappalainen P, Callan-Jones A, Bassereau P. IRSp53 senses negative membrane curvature and phase separates along membrane tubules. Nat Commun. 2015 Oct 15;6:8529. doi: 10.1038/ncomms9529).

(7) Line 117-119: The suggestion that polymer formation between CdvA and CdvB facilitates membrane recruitment is intriguing. However, fluorescence microscopy experiments could better elucidate whether there is sequential recruitment of CdvB followed by CdvA, or if these proteins form a heteropolymer composite for membrane binding. Can CdvB bind membranes independently, or does this require synergy between CdvA and CdvB.

We thank the referee for prompting us to perform this experiment. As we now show in Figure 1C, CdvB indeed is able to bind the membrane independently of CdvA. Whether this happens sequentially or simultaneously is an interesting question, but one that is impossible to address with either the SMS or the flotation assay, because in both cases we can only observe the endpoint of the recruitment.

We would also like to clarify one specific experimental detail. Perhaps unsurprisingly, the results from the flotation assay are dependent on the way the assay is performed. In particular, we observed that the same protein can exhibit a different binding profile depending on whether it is being loaded either at the top or at the bottom of the gradient. This can be seen in Author response image 6. This is counterintuitive, since once the equilibrium is reached, the result should only depend on the density of the sample. We performed an overnight centrifugation (> 16 hours) on a short tube (< 3 cm tall), thus equilibrium is being reached (which is corroborated by the fact that CdvB1 and CdvB2 can float to the top of the gradient within this timespan, as shown in Figure 2C, 2E, 2G). We ascribe the difference between top and bottom loading to the fact that, when the sample is loaded at the bottom, it has to be mixed with a concentrated sucrose solution, while in the case of loading from the top, this is not done.

In literature, both loading from top and from bottom have been used:

- Lata S, Schoehn G, Jain A, Pires R, Piehler J, Gottlinger HG, Weissenhorn W. Helical structures of ESCRTIII are disassembled by VPS4. Science. 2008 Sep 5;321(5894):1354-7. doi: 10.1126/science.1161070

- Moriscot C, Gribaldo S, Jault JM, Krupovic M, Arnaud J, Jamin M, Schoehn G, Forterre P, Weissenhorn W, Renesto P. Crenarchaeal CdvA forms double-helical filaments containing DNA and interacts with ESCRT-III-like CdvB. PLoS One. 2011;6(7):e21921. doi: 10.1371/journal.pone.0021921.

- Senju Y, Lappalainen P, Zhao H. Liposome Co-sedimentation and Co-flotation Assays to Study LipidProtein Interactions. Methods Mol Biol. 2021;2251:195-204. doi: 10.1007/978-1-0716-1142-5_14. In performing the flotation assay for CdvB1 and CdvB2ΔC, or when using all 4 proteins together, we loaded the sample at the bottom, and we could detect reproducible binding to liposomes (Figures 2D, 2F, 2H, 3A). However, CdvB does not bind the membrane when loaded at the bottom. Thus, for the experiments shown in figure 1C, we loaded the proteins at the top. This experimental setup allowed us to highlight that CdvB indeed induce a stronger interaction between CdvA and the membrane.

Author response image 6.

CdvB binding to multilamellar vesicles in a flotation assay. In the left panel, the sample was loaded at the top of the sucrose gradient; in the right panel it was loaded at the bottom.

(8) Line 165-173: The authors claim that filament curvature differs between CdvB2ΔC alone and the CdvB1:CdvB2ΔC complex. Are these differences statistically significant? What is the sample size (N)? Furthermore, how do the authors confirm interactions between these proteins in the absence of membranes based solely on EM micrographs?

We can confirm that the filaments are composed by both proteins, because the filaments have different curvature when both proteins are present. However, as requested by referee 3, point (7), we removed the quantification of curvature from panel 2C. We report the N number in the text.

(9) Line 121-123: Are the authors referring to positive or negative membrane curvatures? The cited literature suggests ESCRT-III proteins either lack curvature preferences (e.g., Snf7, CHMP4B) or prefer high positive curvature (e.g., late ESCRT-III subunits). This is confusing since the authors later test recruitment to negatively curved necks.

We do not claim that Cdv proteins prefer positive or negative curvature, because the necks present in dumbbells have a catenoid geometry, which include both positive and negative curvature. We have now clarified this in the discussion.

(10) Since the conclusions rely on the oligomeric state of the proteins, providing SEC-MALS spectra to show the protein oligomeric state right after the purification would strengthen the claims.

While such SEC-MALDI experiments may be interesting, practical implementation of this is not possible since both first authors left the lab on to new positions.

(11) Line 157-160: Suppl. Fig. 2 shows only a single EM micrograph of a small filament. Could the authors provide lower magnification images showing more filaments?

As requested by Referee 3, point (7), we have toned down the importance of these short filaments.

Also, why are the sample sizes for filament length (N=161) and width (N=129) different?

Protein filaments formed by Cdv tend to stick to each other side by side, so that for some filaments the width could not be accurately assessed, and accordingly those were removed from the analysis.

(12) The introduction states that CdvA binds membranes while CdvB does not. However, the results suggest CdvB facilitates membrane binding, helping CdvA attach. This discrepancy needs further explanation.

We thank the referee for raising this point. We have now performed additional experiments (both SMS assay and flotation assays) showing that indeed CdvB from M. sedula is (unlike CdvB from Sulfolobus) able to bind the membrane on its own (Figure 1C, 1F).

Reviewer #2 (Recommendations for the authors):

Best practice would be to show single fluorescence channels in grayscale or inverted grayscale, retaining pseudocolouring only for the merged multichannel image.

We decided to retain and standardize the colors, both for gels and for microscopy images, in order to have the same color-code for each protein. We believe this improves readability, and this was also a request from Referee 3. Thus, throughout the manuscript, CdvA is in grayscale, CdvB in yellow, CdvB1 in green, CdvB2ΔC in cyan and the membrane in magenta.

It would be great to include a quantification of liposome curvature vs focal intensity of the various Cdv components - across figures.

Quantification of liposome curvature at the neck can be done (De Franceschi et al., Nature Nanotech. 2024). However, in practice, this requires transferring of the sample post-preparation into a new chamber in order to increase the signal-to-noise ratio of the encapsulated dye, a procedure that drastically reduces the yield of dumbbells. The very sizeable amount of work required to obtain reliable measurements, especially considering all the proteins and protein combinations used in this study, indicates that this represents a project in itself, which goes well beyond the scope of this manuscript.

Reviewer #3 (Recommendations for the authors):

(1) We would encourage the authors to consider including the length of the scale bar next to the scale bar in each image and not in the figure description. This would greatly aid in clarity and interpretation of figures.

We have now written the length of the scale bar in the figures.

(2) In a similar vein, could the authors consider labeling panels throughout the manuscript, writing that sample is being presented? This goes mainly for the negative stain and the dumbbell fluorescence images, as having to continuously consult the figure legend again hinders clarity.

We have now labelled the EM images as requested by the referee.

(3) Lines 254-256: would the statement hold not only for CdvB2∆C, but for all imaged proteins? They all seem to localize to membrane necks, presumably favoring membrane binding to a specific membrane topology.

We agree with the referee, and changed the phrasing accordingly.

(4) CdvB2∆C construct - presumably this was a truncation of helix 5 of the ESCRT-III domain? Figure 1A shows that the ESCRT-III domain spans residues 34-170 and therefore implies that all five ESCRT-III helices (which make up the ESCRT-III domain) are present in the C-terminal truncation. Could the authors clarify?

Indeed, the truncation was done at residue 170.

(5) Results of the liposome flotation assays are presented inconsistently across the three figures (Figs 1C, 2DFH, and 3A). This makes it more difficult than it needs to be to interpret and compare results. Could the authors consider presenting the three gels in a more similar, standardized way across the three figures?

To improve readability, we now standardized the colors, both for gels and for microscopy images, in order to have the same color-code for each protein. Thus, throughout the manuscript, CdvA is in grayscale, CdvB in yellow, CdvB1 in green, CdvB2ΔC in cyan and the membrane in magenta.

(6) From the data presented in Fig 1EF, it cannot be concluded whether CdvB and CdvA colocalize, as only one protein is labelled. Is there a technical reason for this?

We have now repeated the same experiment by having both proteins labelled, confirming that there is co-localization at the neck (Figure 1G).

(7) Fig 2C: is the difference between the two samples significant

As requested by Referee 3, we have removed Figure 2C.

(8) Fig 2I is missing a 'merged' panel.

We have now added the merged panel.

(9) The fluorescence intensity plots in Supp Figs 1C and 3C would be easier to interpret if the lipid and protein signal would be plotted on the same plot (say, with normalized fluorescence intensity)

It is not immediately obvious to us what the signal should be normalized to. What we wished to convey with these plots was that the intensity of proteins spikes at the neck region. In an attempt to improve clarity, we have now aligned the plots vertically, and highlighted the position of the neck.

(10) CdvA should have a capital "A" in Figure 3A, panel 3.

We have now corrected this.

(11) The discussion doesn't comment on the need to truncate CdvB2.

This is explained in the result session.

Reviewer #2 (Public review):

Summary:

This study systematically characterizes the activity patterns of a lateral supramammillary nucleus (SuM)-medial septum (MS)-hippocampus circuit across sleep-wake cycles and its role in memory consolidation. The authors demonstrate that the lateral SuM-MS projection is specifically active during REM sleep, and that REM-selective inhibition of this circuit, and of its downstream MS-CA2 pathway, impairs the consolidation of social memory. The work is well-designed, and the data are robust in supporting clear and significant conclusions. It provides important new insights into how distinct memory modalities could be processed by parallel, sleep-active subcortical-hippocampal circuits. The manuscript is of high quality overall, with some points to address as detailed below.

Strengths:

(1) Novel finding:<br /> The identification of a REM-specialized subpopulation within the lateral SuM-MS pathway and its specific role in social memory consolidation via the lateral SuM-MS-CA2 projection is a significant advance. It effectively complements the previously described direct SuM-CA2 pathway and supports a model of the SuM as a "REM-hub" routing information through dedicated downstream targets.

(2) Technical rigor:<br /> The combination of retrograde tracing, in vivo calcium imaging, single-unit identification via optrode recording, and temporally precise (REM-sleep-specific) optogenetic manipulation provides strong correlative and causal evidence.

(3) Appropriate controls:<br /> Behavioral experiments include crucial controls for optogenetic inhibition (GtACR1 group, NREM/Wake inhibition control, mCherry control), effectively ruling out nonspecific effects of light or timing.

Weaknesses:

(1) Figure titles/descriptions:<br /> For clarity, the authors should consider specifying the recording method in the figure titles or legends. For instance, Figure 2: "Bulk Ca2+ activity (fiber photometry) of lateral SuM-MS projecting neurons..." and Figure 3: "Single-unit activity patterns (optrode recordings) of lateral SuM-MS projecting neurons...".

(2) Statistical details:<br /> The use of "LSD post-hoc comparison" following ANOVA is noted. LSD is sensitive but can increase Type I error risk with multiple comparisons. Please justify its use or consider employing a more conservative post-hoc test (e.g., Tukey's or Bonferroni) for key comparisons like the social preference index in Figure 4h to bolster robustness.

(3) Data presentation:<br /> When reporting statistical results in figure legends (e.g., Figures 2d, 3i-k), please provide the specific test statistic values (e.g., F, χ²) and exact P values where possible, rather than only significance asterisks.

(4) Deepening mechanistic insight:<br /> The study excellently demonstrates "what" the circuit does. The discussion could be strengthened by further exploring "how" it might work. The finding that SuM-MS inhibition does not affect CA1 theta power is interesting and distinguishes it from other MS/hippocampal pathways. The suggestion of a theta-independent mechanism is plausible. Could the authors hypothesize more specifically? For example, might this circuit modulate reactivation events in the local CA2 network, neurochemical milieu (e.g., acetylcholine), or synapse-specific plasticity during REM sleep to facilitate social memory consolidation?

(5) Implications of regional heterogeneity:<br /> The functional divergence between lateral (90% REM-active) and medial SuM-MS neurons is intriguing. A brief discussion on the potential anatomical basis (differential inputs/outputs) and functional significance (e.g., integration of specific affective or arousal signals) of this subdivision would be valuable.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Kroeg et al. describe a novel method for 2D culture human induced pluripotent stem cells (hiPSCs) to form cortical tissue in a multiwell format. The method claims to offer a significant advancement over existing developmental models. Their approach allows them to generate cultures with precise, reproducible dimensions and structure with a single rosette; consistent geometry; incorporating multiple neuronal and glial cell types (cellular diversity); avoiding the necrotic core (often seen in free-floating models due to limited nutrient and oxygen diffusion). The researchers demonstrate the method's capacity for long-term culture, exceeding ten months, and show the formation of mature dendritic spines and considerable neuronal activity. The method aims to tackle multiple key problems of in vitro neural cultures: reproducibility, diversity, topological consistency, and electrophysiological activity. The authors suggest their potential in high-throughput screening and neurotoxicological studies.

Strengths:

The main advances in the paper seem to be: The culture developed by the authors appears to have optimal conditions for neural differentiation, lineage diversification, and long-term culture beyond 300 days. These seem to me as a major strength of the paper and an important contribution to the field. The authors present solid evidence about the high cell type diversity present in their cultures. It is a major point and therefore it could be better compared to the state of the art. I commend the authors for using three different IPS lines, this is a very important part of their proof. The staining and imaging quality of the manuscript is of excellent quality.

We thank the reviewer for the positive comments on the potential of our novel platform to address key problems of in vitro neural culture, highlighting the longevity and reproducibility of the method across multiple cell lines.

Weaknesses:

(1) The title is misleading: The presented cultures appear not to be organoids, but 2D neural cultures, with an insufficiently described intermediate EB stage. For nomenclature, see: doi: 10.1038/s41586-022-05219-6. Should the tissue develop considerable 3D depth, it would suffer from the same limited nutrient supply as 3D models - as the authors point out in their introduction.

We appreciate the opportunity to clarify this point. We respectfully disagree that the cultures do not meet the consensus definition of an organoid. In fact, a direct quote from the seminal nomenclature paper referenced by the reviewer states: “We define organoids as in vitro-generated cellular systems that emerge by self-organization, include multiple cell types, and exhibit some cytoarchitectural and functional features reminiscent of an organ or organ region. Organoids can be generated as 3D cultures or by a combination of 3D and 2D approaches (also known as 2.5D) that can develop and mature over long periods of time (months to years).” (Pasca et al, 2022 doi10.1038/s41586-022-05219-6). Therefore, while many organoid types indeed have a more spherical or globular 3D shape, the term organoid also applies to semi-3D or nonglobular adherent organoids, such as renal (Czerniecki et al 2018, doi.org/10.1016/j.stem.2018.04.022) and gastrointestinal organoids (Kakni et al 2022, doi.org/10.1016/j.tibtech.2022.01.006). Accordingly, the adherent cortical organoids described in the manuscript exhibit self-organization to single radial structures consisting of multiple cell layers in the z-axis, reaching ~200um thickness (therefore remaining within the limits for sufficient nutrient supply), with consistent cytoarchitectural topology and electrophysiological activity, and therefore meet the consensus definition of an organoid.

(2) The method therefore should be compared to state-of-the-art (well-based or not) 2D cultures, which seems to be somewhat overlooked in the paper, therefore making it hard to assess what the advance is that is presented by this work.

It was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods. Compared to stateof-the-art 2D neural network cultures, adherent cortical organoids provide distinct advantages in:

(1) Higher order self-organized structure formation, including segregation of deeper and upper cortical layers.

(2) Longevity: adherent cortical organoids can be successfully kept in culture for at least 1 year, whereas 2D cultures typically deteriorate after 8-12 weeks.

(3) Maturity, including the formation of dendritic mushroom spines and robust electrophysiological activity.

(4) Cell type diversity including a more physiological ratio of inhibitory and excitatory neurons (10% GAD67+/NeuN+ neurons in adherent cortical organoids, vs 1% in 2D neural networks), and the emergence of oligodendrocyte lineage cells.

On the other hand, limitations of adherent cortical organoids compared to 2D neural network cultures include:

(1) Culture times for organoids are much longer than for 2D cultures and the method can therefore be more laborious and more expensive.

(2) Whole cell patch clamping is not easily feasible in adherent cortical organoids because of the restrictive geometry of 384-well plates.

(3) Reproducibility is prominently claimed throughout the manuscript. However, it is challenging to assess this claim based on the data presented, which mostly contain single frames of unquantified, high-resolution images. There are almost no systematic quantifications presented. The ones present (Figure S1D, Figure 4) show very large variability. However, the authors show sets of images across wells (Figure S1B, Figure S3) which hint that in some important aspects, the culture seems reproducible and robust.

We made considerable efforts to establish quantitative metrics to assess reproducibility. We applied a quantitative scoring system of single radial structures at different time points for multiple batches of all three lines as indicated in Figure S1C. This figure represents a comprehensive dataset in which each dot represents the average of a different batch of organoids containing 10-40 organoids per batch. To emphasize this, we have adapted the graph to better reflect the breadth of the dataset. Additional quantifications are given in Figure S2 for progenitor and layer markers for Line 1 and in Figure 2 for interneurons across all three lines, showing relatively low variability. That being said, we acknowledge the reviewer’s concerns and have modified the text to reduce the emphasis of this point, pending more extensive data addressing reproducibility across an even broader range of parameters.

(4) What is in the middle? All images show markers in cells present around the center. The center however seems to be a dense lump of cells based on DAPI staining. What is the identity of these cells? Do these cells persist throughout the protocol? Do they divide? Until when? Addressing this prominent cell population is currently lacking.

A more comprehensive characterization of the cells in the center remains a significant challenge due to the high cell density hindering antibody penetration. However, dyebased staining methods such as DAPI and the LIVE/DEAD panel confirm a predominance of intact nuclei with very minimal cell death. The limited available data suggest that a substantial proportion of the cells in the center are proliferative neural progenitors, indicated by immunolabeling for SOX2 (Figure 2A,D;Figure S4C). Furthermore, we are currently optimizing the conditions to perform single cell / nuclear RNA sequencing to further characterize the cellular composition of the organoids.

(5) This manuscript proposes a new method of 2D neural culture. However, the description and representation of the method are currently insufficient. (a) The results section would benefit from a clear and concise, but step-by-step overview of the protocol. The current description refers to an earlier paper and appears to skip over some key steps. This section would benefit from being completely rewritten. This is not a replacement for a clear methods section, but a section that allows readers to clearly interpret results presented later.

We have revised the manuscript to include a more detailed step-by-step overview of the protocol.

(b) Along the same lines, the graphical abstract should be much more detailed. It should contain the time frames and the media used at the different stages of the protocol, seeding numbers, etc.

As suggested, we have adapted the graphical abstract to include more detail.

Reviewer #2 (Public review):

Summary:

In this manuscript, van der Kroeg et al have developed a method for creating 3D cortical organoids using iPSC-derived neural progenitor cells in 384-well plates, thus scaling down the neural organoids to adherent culture and a smaller format that is amenable to high throughput cultivation. These adherent cortical organoids, measuring 3 x 3 x 0.2 mm, self-organize over eight weeks and include multiple neuronal subtypes, astrocytes, and oligodendrocyte lineage cells.

Strengths:

(1) The organoids can be cultured for up to 10 months, exhibiting mature dendritic spines, axonal myelination, and robust neuronal activity.

(2) Unlike free-floating organoids, these do not develop necrotic cores, making them ideal for high-throughput drug discovery, neurotoxicological screening, and brain disorder studies.

(3) The method addresses the technical challenge of achieving higher-order neural complexity with reduced heterogeneity and the issue of necrosis in larger organoids. The method presents a technical advance in organoid culture.

(4) The method has been demonstrated with multiple cell lines which is a strength.

(5) The manuscript provides high-quality immunostaining for multiple markers.

We appreciate the reviewer’s acknowledgement of the strengths of this novel platform as a technical advance in organoid culture that reduces heterogeneity and shows potential for higher throughput experiments.

Weaknesses:

(1) Direct head-to-head comparison with standard organoid culture seems to be missing and may be valuable for benchmarking, ie what can be done with the new method that cannot be done with standard culture and vice versa, ie what are the aspects in which new method could be inferior to the standard.

In our opinion, it would be extremely difficult to directly compare methods. Most notably, whole brain organoids grow to large and irregular globular shapes, while adherent cortical organoids have a more standardized shape confined by the geometry of a 384well. Moreover, it was not our intention to benchmark this model quantitatively against other culture systems. Rather, we have attempted to characterize the opportunities and limitations of this approach, with a qualitative contrast to other culture methods, as addressed in response to comment 2 of Reviewer 1 above.

(2) It would be important to further benchmark the throughput, ie what is the success rate in filling and successfully growing the organoids in the entire 384 well plate?

Figure S1 shows the success rate of organoid formation and stability of the organoid structures over time. In addition, we have added the number of wells that were filled per plate.

(3) For each NPC line an optimal seeding density was estimated based on the proliferation rate of that NPC line and via visual observation after 6 weeks of culture. It would be important to delineate this protocol in more robust terms, in order to enable reproducibility with different cell lines and amongst the labs.

Figure S1 provides the relationship between proliferation rate and seeding density, allowing estimation of seeding densities based on the proliferation rate of the NPCs. However, we appreciate the reviewers' feedback and have modified the methods to provide more detail.

Reviewer #3 (Public review):

Summary:

Kroeg et al. have introduced a novel method to produce 3D cortical layer formation in hiPSC-derived models, revealing a remarkably consistent topography within compact dimensions. This technique involves seeding frontal cortex-patterned iPSC-derived neural progenitor cells in 384-well plates, triggering the spontaneous assembly of adherent cortical organoids consisting of various neuronal subtypes, astrocytes, and oligodendrocyte lineage cells.

Strengths:

Compared to existing brain organoid models, these adherent cortical organoids demonstrate enhanced reproducibility and cell viability during prolonged culture, thereby providing versatile opportunities for high-throughput drug discovery, neurotoxicological screening, and the investigation of brain disorder pathophysiology. This is an important and timely issue that needs to be addressed to improve the current brain organoid systems.

We thank the reviewer for highlighting the strengths of our novel platform. We appreciate that all three reviewers agree that the adherent cortical organoids presented in this manuscript reliably demonstrate increased reproducibility and longevity. They also commend its potential for higher throughput drug discovery and neurotoxicological/phenotype screening purposes.

Weaknesses:

While the authors have provided significant data supporting this claim, several aspects necessitate further characterization and clarification. Mainly, highlighting the consistency of differentiation across different cell lines and standardizing functional outputs are crucial elements to emphasize the future broad potential of this new organoid system for large-scale pharmacological screening.

We appreciate the feedback and have added more detail on consistency and standardization of functional outputs.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Minor points

(1) As the preprint is officially part of the eLife review, I have to remark that the preprint which is made available on bioarxiv, suffers from some serious compatibility or format problem: one cannot highlight sentences as in a regular PDF and when trying to copypaste sentences from it jumbled characters are copied to the clipboard.

The updated version of the paper on bioRxiv should not suffer from these compatibility issues.

(2) Since the paper is presenting a new method it should briefly describe how each step, including the hiPSC culture was done, the reference to an earlier publication in this case is not sufficient, and this practice is generally best to avoid for methods papers.

Each step in the culturing process has now been described in the methods.

(3) The EB stage is insufficiently described. The "2D - 3D - 2D" transitions should be clearly explained.

The methods section has been rewritten and expanded to include these processes in more detail.

(4) Is there one FACS sorting in the protocol, or multiple (additional at IPS culture)? What markers each? What is the motivation for sorting and purifying the neural progenitors? Was the culture impure? What was purity? What cell types are expected after sorting, and what is removed?

Only one FACS sorting step is performed at the NPC stage. This was added as an improvement to our original neural network protocol (Günhanlar et al 2018) to ensure consistency over different hiPSC source cell lines that can yield variable amounts of frontal cortical patterned NPCs. Positive sorting for neural lineage markers CD184 and CD24, and negative sorting for mesenchymal/neural crest CD217 and CD44 glial progenitor markers, according to Yuan et al 2011, ensures frontal-patterned cortical NPCs as confirmed for all batches by immunohistochemistry for SOX2, Nestin and FOXG1. We have added new text to the Methods section to clarify this more explicitly.

(5) Seeding protocol and parameters are insufficiently described, and from what I read they are poorly defined: "Specifically, the optimal seeding density was determined by visual inspection of the organoids between 28 to 42 days after seeding a range of cell densities in the 384-well plate wells." For a new method, precise, actionable instructions are needed. I may have overlooked those elsewhere, in this case, please clarify these sections.

The Methods section was rewritten and expanded to describe the methodology in greater detail with more actionable instructions.

(6) The timeline in Figure 1 is not clearly delineated; I found it hard to understand which figure corresponds to which stage (e.g. facs sorting is not mentioned in the first part of the results but it is part of Figure 1A, neural rosette formation can happen both before and after facs sorting, simply referring to rosettes is not clear). Later parts of the manuscript 
> clearly introduce the terms sorting and seeding in the context of this method, and how ages (days) refer to these time points.

Figure 1 was adapted to clarify the generation of Neural Progenitor Cells (NPCs) and subsequent seeding of NPCs to generate Adherent Cortical Organoids (ACOs).

(7) The authors define: "cortical organized defined as a single radial structure." This is not a commonly used definition of organoids, for nomenclature, please see: doi: 10.1038/s41586-022-05219-6 (Pasca et al 2022).

To clarify, the statement is not meant to reflect a definition of organoids in general, but rather the scoring of proper structure formation for Figure S1C. For discussion on nomenclature, see our response to point 1 of Reviewer 1 in the public review. We changed the wording to be more accurate.

(8) In Figure S1d, the authors write: "the fraction of structurally intact cultures decreased to 50%", but I'm looking at that graph there seems to be no notable decrease, but huge variability. The authors should quantify claims of decrease by linear regression and an R square. Variation within and the cross-cell lines seem to be large. Also, it is unclear if dots are corresponding to the same wells/plates, in other words: is this a longitudinal experiment? What is the overall success rate? How is success determined? Are there clear criteria? to the same wells/plates, in other words: is this a longitudinal experiment? What is the overall success rate? How is success determined? Are there clear criteria?

We agree with the reviewer that the claim on fraction of intact cultures decreasing over time to 50% is an overinterpretation due the large variability. We changed the wording in the manuscript to: While some later batches show moderately reduced success rates compared with the earliest batches, properly formed single-structure organoids were still obtained at 40–90% success across all examined time points (Figure S1C), indicating that long-term culture is feasible albeit with variable efficiency. The data are not longitudinal as each dot represents an endpoint of a different batch of organoids, totaling 18 independent batches across the three lines. We have clarified this in the figure legend. Success was defined at the well level as the presence of a single, continuous radial structure occupying the well, without obvious fragmentation or fusion events, as assessed by LIVE/DEAD that also confirmed viability. Wells were scored as successful only when the radial structure showed predominantly live signal with no large necrotic areas. Wells containing multiple radial structures, fused aggregates, or predominantly dead tissue were scored as unsuccessful.

(9) Figure s1c: the numbering to this panel should be swapped, because it is referenced after other panels in the text. The reference is confusing: "Plotting the interaction between proliferation and the amount of NPCs required to be seeded for the successful generation of adherent cortical organoids" - success is not present in this graph at all? How is that measured?

Figures S1C and S1D have been adapted to clarify the measure of ‘successful organoid formation’.

(a) The description of this plot is confusing: "The doubling time of the NPCs explains more than half the variation (r2 = 0.67) of the required seeding density." What else is there? I thought that this was the formula the authors suggested to determine seeding density, but it seems not. Or is "manual inspection" the determinant, and that seems to correlate with this metric?

Even though the rate of proliferation, measured as doubling time, is the main determinant of the seeding density, it is not the only determinant of the seeding density. For instance, intrinsic differences in differentiation potential could also play a role. Therefore, NPC lines with similar doubling times might still have slightly different optimal seeding densities. We have added clarification of this conclusion to the Results section.

(b) Seeding density is a key parameter in many in vitro differentiation and culture protocols. This importance however does not mean that this density is attributable to differences in cell proliferation rate. Alternatively, the amount of cells determines the amount of secreted molecules and cell-to-cell contacts.

Here, when we refer to the cell density, we specifically refer to the cell density needed to generate the ACO. We show that the most important contributor to the variation in ACO formation is the proliferation, measured here as the doubling time. We agree that there are other factors involved such as the secreted molecules, cell-to-cell contacts as well as the ability of a given NPC line to differentiate into a post-mitotic cell.

(c) Is it mentioned which cell line this experiment corresponds to?

The data in Figure S1D is from the 3 reported cell lines, as well as 2 clones from a fourth IPS cell line. This is detailed in the Methods section of the proliferation assay.

(d) Without a more detailed explanation, seeding density and doubling time could be independent variables.

These two variables are highly correlated as shown in Figure S1D, but it is true that there can be other variables that account for the observed variance, as discussed above in Point 9b.

(e) In this figure the success rate is not visible at all so I have no idea how the autors arrive at a conclusion about success rate.

We have adapted the figure legend to reflect which cell lines the dots in Fig. S1D represent. NPC lines can have substantial variation in proliferation rates. The figure reflects data of NPCs of 5 clones of 4 different hiPSC lines (as indicated in the Methods) with different proliferation rates. Also, the ACO success rate (operationally defined uniformly to the data shown in Fig. S1C) was also included.

(10) Figure 2: Clean spatial segregation seems to be a strength of the system and therefore I would recommend putting more of the relevant microscopy images to the main figure, which are now currently in Figure S4.

We have adapted Figure 2 accordingly, and included additional representative cortical layering images in Figure S4.

(11) The variability in interneuron content seems to be significant, as currently presented in the figure. However, this may be due to a special organization. It would first quantify in consecutive rings around the centers whether interneurons have a tendency to be enriched towards the center or the edge of the culture. Maybe this explains the variability that is currently present in Figure s5b.

We agree that spatial organization of interneurons could, in principle, contribute to variability. In our analysis, however, images were acquired from positions selected by a random sampling grid across the entire culture, rather than from specific central or peripheral regions. Each field contained on average 130.6 ± 16.1 NeuN+ nuclei, which provided a relatively large sampling volume per position. If interneurons were strongly enriched at the center or edge, we would expect systematic differences in interneuron fraction between fields assigned to central versus peripheral grid positions. We did not observe such a pattern in our dataset, suggesting that spatial organization is not the main driver of the observed variability.

(12) Because in previous figures it seems like there is considerable variability across individual cultures and images here are coming from separate cultures, please use different shapes of the points coming from different cultures/wells, to see if maybe there is a culture-to-culture difference that explains the variability present in the figure.

We have added different symbols per organoid for the interneuron quantifications and moved this quantification to main Figure 2.

(13) I believe it is currently the standard error of the mean which is displayed in the figure, which is not an appropriate representation for variability, or the reproducibility across individual data points. SEM quantifies the reproducibility of the mean, not the reproducibility of the individual data points, which matters here. Mean refers to the mean of this quantification experiment and therefore it's not a biological entity. A box plot showing the interquartile range besides the individual data points would be an accurate representation of the spread of the data.

We agree and have adapted the data, now in Figure 5, accordingly.

(14) Again, in general, the main figures should contain much more of the quantification, as opposed to just raw images.

Quantifications have been added in Figure 2 for the GAD67/NeuN for all cell lines as well as a time course quantification of GAD67/NeuN for 1 of the cell lines. In Figure 4, we have added excitatory and inhibitory synaptic quantifications.

(15) Figure 2F-I the location of the center of the rosette should be marked with a star so that the conclusion about the direction of processes can be established.

The suggested addition of a marker at the center of each rosette was evaluated but not implemented, because it reduced rather than improved figure clarity.

(16) Figure 3 b and c:

High magnification images of single cells, can't show changes in cell type morphology, and one cannot conclude that these cells are present in significant numbers across time. Zoomed-out images or quantification would be necessary for such a claim. The authors already have such images as presented in the next panels, so quantification without new experiments.
> I am uncertain about the T3 supplement here - do these images correspond to the same conditions?

(a) It is unclear to me why different markers are used in the different panels, namely why NG2 is not used in any of the other images.

NG2 was used at early developmental time points to show the presence of Oligodendrocyte Precursor Cells (OPCs). At later time points, the focus switched to MBP staining to indicate more mature oligodendrocyte lineage cells. Although NG2 and MBP are not in the same panels, the staining was performed for both antibodies at the same developmental time point (Day 119) as seen in Figure 3C and 3D.

(b) Color coding in Figure 3G is ambiguous; the use of two blues should be avoided, and the Sub-sub panels should be individually labeled for the color code.

We agree, and have now used different colors.

(c) It is unclear if the presence of the t3 molecule is part of the standard procedure or if it was a side experiment to enhance the survival of oligodendrocytes. Are there no oligodendrocytes without? How does T3 affect other cell types, and the general health and differentiation of the cultures?

Indeed, T3 is essential for oligodendrocyte formation. We did not observe obvious effects on the general health or differentiation potential of the cultures.

(d) Is the 2ng/ml t3 from day one to the final day?

Indeed, in the organoids cultured to study oligodendrocyte formation, T3 was added from Day 1. These details have now been clarified in the Methods and Results sections.

(17) Figure 4:

(a) Microscopy in this figure is high quality and very convincing about neural maturity.

(b) The term "cluster" should be avoided. Unclear what it means here, but my best guess is "cells in a frame of view." Cluster is used with a different meaning in electrophysiology.

This was adapted to ‘neurons in a field of view (FOV)’.

(c) Panel J: I assume each row corresponds to a single cell? Could this be clarified? Are these selected cells from each frame, or all active cells are represented?

Indeed, each row corresponds to a single cell, showing all active cells in the frame. This is now clarified in the legend.

(d) How many Wells do these data correspond to, and in which line it was measured?

As reported in the legend for Figure 5, these data correspond to 2 wells at Day 61 to which we have now added calcium imaging data from 3 wells from a different batch at Day 100. We have included in the legend that these recordings were from Line 1.

(e) Panels G to I, again, the use of standard error of the mean is inappropriate and misleading: looking at the error bar one must conclude that there is minimal variation, which is the exact opposite of the conclusions, when one would look at the variability of the raw data points.

As suggested, the graphs have been adapted as boxplots with interquartile ranges to highlight the distribution of data points.

(f) It is unclear how many neurons and how many total actively firing neurons are present in the videos analyzed

All neurons that were active in the field of view and showed at least one calcium event during the ~10 minute recording were included in the analysis. Using this method, we cannot comment on the proportion of neurons that were active from the total amount of neurons present, since the AAV virus we used does not transduce all neurons.

(g) This figure shows the strength of the method in achieving neural maturity and function. There seems to be that there is considerable activity in the neuronal cultures analyzed. To conclude how reliably the method leads to such mature cultures one would need to measure at least a dozen wells (even if with some simpler and low-resolution method). Concluding reproducibility from one or two hand-picked examples is not possible.

We agree with the reviewer that the number of wells used for calcium imaging analysis was limited. We are currently working on more advanced methods to increase the throughput of this analysis. However, we’ve now added another timepoint to the calcium imaging data in Figure 5 from an independent batch of 3 adherent cortical organoids, which demonstrates continued robust activity at Day 100, as well as Day 61.

Methods:

(1) Stem cell culture. The artist described that line 3 is grown on MEFs. Is this true for the other two lines, furthermore were they cultured in identical conditions?

Line 2 and 3 were not grown on MEFs. We specifically chose different sources of NPCs to reflect the robust nature of the differentiation protocol. We have recently also adapted the protocol from Line 3 NPCs to confirm that the protocol also works starting from hiPSCs grown in feeder-free conditions in StemFlex medium, by adapting NPC differentiation according to our recent publication in Frontiers in Cellular Neuroscience (Eigenhuis et al 2023).

(2) "NPCs were differentiated to adherent cortical organoids between passages 3 and 7 after sorting." Please clarify this sentence. I assume it refers to the first facs sorting of the protocol, but a section is not sufficiently detailed.

We have adapted the methods to clarify that the FACS purification step occurs at the NPC stage.

(3) I didn't fully understand: It seems to be that there are two steps of fact sorting involved, one after passage 3 and one after week 4. This should be represented in the graphical abstract of Figure 1.

As outlined above, there is only 1 FACS sorting step at NPC stage. We have adapted this in the Methods and in the graphical abstract.

(4) Neural differentiation: The authors write that optimal seeding density was determined by visual inspection of the organoids - this is.

We have clarified the Methods section to better explain the process of optimizing the seeding density for each NPC line to generate the ACOs.

(5) What does the following sentence mean: "Cells were refreshed every 2-3 days." Does it mean in replacement of the complete media? How much Media was added to the Wells?

This is a very good point that we have now clarified in the Methods, as full replenishment of media is neither feasible, nor desirable. From the total volume of 110 µl per well, 80 µl is taken out and replaced with 85 µl to compensate for evaporation.

(6) Calcium imaging: can the authors explain the decision to move the cultures one day before imaging into brainphys neural differentiation medium? In 3D organoid protocols, brainphys is gradually introduced to avoid culture shock (very different composition), and used for multiple months to enhance neural differentiation. For recording electrophysiological activity, artificial CSF is the most common choice.

Indeed, for whole cell recordings of 2D neural networks as performed in Günhanlar et al 2018, we used gradual transition to aCSF. For the current ACOs, we found that using BrainPhys from the start of organoid differentiation prevents structure formation, probably because of increased speed of maturation disrupting proliferation and organization of radial glia differentiation. However, by changing the media to BrainPhys just one day before recording (reflecting a gradual change as not all medium is fully replenished and easier than switching to aCSF during recording), we saw greatly improved neuronal activity.

(7) Statistical analysis : As I pointed out before, the standard error of the mean is not an appropriate metric to represent the variability of the data. It is meant to represent the variability of the estimated average. The following thought experiment should make it clear: I measured the expression of a gene in my system. 50 times I measured 0 and 50 times I measured 100. The average is 50, but of course it is a very bad representation of the data because no such data points exist with that value. Yet the standard error of the mean would be plus minus 5.

We have revised Figures 5C–5D to boxplots displaying the interquartile range with all individual data points overlaid, which more accurately represents the variability in the dataset.

Discussion

(1) The discussion focuses on human cortical development, however, the methods presented by the authors entail dissociation and replating through multiple stages not part of brain development. I see the approach as more valuable as a possibly reliable method that generates both diverse and mature neural cultures.

We have revised the Discussion to avoid explicitly invoking an in vitro recapitulation of human cortical development. Nevertheless, given that the NPCs from which the organoids originate exhibit frontal cortical identity, coupled with the timely emergence of cortical neuronal markers and rudimentary cortical layering, we are increasingly confident that the development of these cultures most likely mirrors that of the frontal cortex. To further substantiate this hypothesis, single-cell RNA sequencing experiments will be conducted in the future to provide additional insights.

(2) One of the major claims of the authors is that the method is very reproducible. However, there is almost no data on reproducibility throughout the paper. Mostly single, high magnification images are presented, which therefore represent a small region of a single well of a single batch of a single cell line. Based on the data presented it is not possible to evaluate the reproducibility of the method.

We agree that the original version did not sufficiently document reproducibility. To address this, we have refined and expanded our presentation of reproducibility data. The previous success-rate panel (original Figure S1D) has been moved and adapted as the new Figure S1C. In this updated version, each dot still represents the endpoint success rate of an independent batch, but dot size now scales with batch size (10–40 organoids), and the legend specifies the total numbers of organoids analyzed per line (line 1: n=248; line 2: n=70; line 3: n=70). Together with the distribution of success rates between ~40– 90% across multiple time points and three iPSC lines, this more detailed representation allows readers to directly assess the robustness of line-to-line and batch-to-batch performance. In addition, new time course quantifications of interneuron proportion (Figure 2G,H), synaptic marker densities (Figure 4H, I), and late-stage calcium imaging (Figure 5C,D,E) further demonstrate that key structural and functional read-outs show overlapping ranges across lines and independent differentiations, reinforcing that the method yields reproducible core phenotypes despite some biological variability.

(3) The data presented is very promising, and it suggests that the authors derived optimal conditions for neural differentiation and neural culture diversification. I am confident that the authors can show that reproducibility, at least in a practical sense (e.g. in wells that form a culture) is high.

Overall, this is a very promising and exciting work, that I am looking forward to reading in a mature manuscript.

Reviewer #2 (Recommendations for the authors):

(1) Direct head-to-head comparison with standard organoid culture seems to be missing and may be valuable for benchmarking, ie what can be done with the new method that cannot be done with standard culture and vice versa, ie what are the aspects in which new method could be inferior to the standard.

We have now more clearly elaborated the differences with other methods. As addressed in our response to point 2 of Reviewer 1 in the public reviews, there are several limitations and advantages to the adherent cortical organoids model listed as follows:

Advantages of adherent cortical organoids:

(1) Higher order self-organized structure formation, including segregation of deeper and upper cortical layers.

(2) Longevity: adherent cortical organoids can be successfully kept in culture for at least 1 year, whereas 2D cultures typically deteriorate after 8-12 weeks.

(3) Maturity, including the formation of dendritic mushroom spines and robust electrophysiological activity.

(4) Cell type diversity including a more physiological ratio of inhibitory and excitatory neurons (10% GAD67+/NeuN+ neurons in adherent cortical organoids, vs 1% in 2D neural networks), and the emergence of oligodendrocyte lineage cells.

On the other hand, limitations of adherent cortical organoids compared to 2D neural network cultures include:

(1) Culture times for organoids are much longer than for 2D cultures and the method can therefore be more laborious and more expensive.

(2) Whole cell patch clamping is not easily feasible in adherent cortical organoids because of the restrictive geometry of 384-well plates.

(2) It would be important to further benchmark the throughput, ie what is the success rate in filling and successfully growing the organoids in the entire 384 well plate?

We have addressed this question in the current version of Fig. S1C, in which multiple batches of organoids of all three lines were scored for their success rate. The graph reflects the proportion of properly formed organoids of +/- 400 seeded wells scored at different timepoints, in which each timepoint is a different batch. As mentioned in the response to Reviewer 1, we have also added data on the number of organoids seeded per line in the figure legend.

(3) For each NPC line an optimal seeding density was estimated based on the proliferation rate of that NPC line and via visual observation after 6 weeks of culture. It would be important to delineate this protocol in more robust terms, in order to enable reproducibility with different cell lines and amongst the labs.

As outlined in the response to Reviewer 1, we have clarified the Methods and Discussion sections on seeding density and proliferation rate.

Reviewer #3 (Recommendations for the authors):

Kroeg et al. have introduced a novel method to produce 3D cortical layer formation in hiPSC-derived models, revealing a remarkably consistent topography within compact dimensions. This technique involves seeding frontal cortex-patterned iPSC-derived neural progenitor cells in 384-well plates, triggering the spontaneous assembly of adherent cortical organoids consisting of various neuronal subtypes, astrocytes, and oligodendrocyte lineage cells. Compared to existing brain organoid models, these adherent cortical organoids demonstrate enhanced reproducibility and cell viability during prolonged culture, thereby providing versatile opportunities for high-throughput drug discovery, neurotoxicological screening, and the investigation of brain disorder pathophysiology. This is an important and timely issue that needs to be addressed to improve the current brain organoid systems. While the authors have provided significant data supporting this claim, several aspects necessitate further characterization and clarification. Particularly, highlighting the consistency of differentiation across different cell lines and standardizing functional outputs are crucial elements to emphasize the future broad potential of this new organoid system for large-scale pharmacological screening.

(1) Considering the emergence of astrocyte markers (GFAP, S100b) and upper layer neuron marker (CUX1) around Day 60, the overall differentiation speed is significantly faster compared to other forebrain organoid protocols. Are these accelerated sequences of neurodevelopment consistent across different hiPSC lines?

As shown in Fig. S5, astrocytes are present around Day 60 for all three lines. For comparison with other organoid protocols, an important consideration is that the timeline for these organoids starts at NPC plating, while for other protocols timing often starts from the hiPSC stage. We have clarified the timeline in the graphical abstract in Figure 1A and in the Methods.

(2) The calcium imaging results in Figure 4G were recorded at a single time point, Day 61, a relatively early time window compared to other forebrain organoid protocols (more than 100 days, PMID: 31257131; PMID: 36120104). Are the neurons in adherent cortical organoids functionally mature enough around Day 61? How consistent is this functional activity across different cell lines and independent differentiation batches?

As discussed above in Point 1, it is important to consider that the specified timeline starts from NPC plating. In analogy to 2D neural networks, robust neuronal activity can be observed after ~8 weeks in culture. In addition, we have now added calcium imaging data for an additional batch of organoids at Day 100 in Figure 5, which exhibit comparable levels of neuronal activity as observed on Day 61.

(3) Along the same line, Various cell types, such as oligodendrocytes and astrocytes, are believed to influence neuronal maturation. Therefore, longitudinal studies until the late stage are necessary to observe changes in electrophysiological activity based on the degree of neuronal maturation (at least two more later time points, such as 100 days and 150 days).

As described in the previous points, we have now included a Day 100 time point in the calcium imaging data, in addition to the recordings at Day 61 (Figure 5C-E).

(4) The authors assert that heterogeneity among organoids has been diminished using the human adherent cortical organoids protocol. However, there is inadequate quantitative data to prove the consistency of neuronal activities between different wells. Therefore, experiments quantifying the degree of heterogeneity between organoids, such as through methods like calcium imaging, are necessary to determine if neuron activity occurs consistently across each organoid well.

We agree with the review and have added several quantitative experiments: a) we’ve added another timepoint to the calcium imaging data in Figure 5 from an independent batch of 3 adherent cortical organoids, which demonstrates continued robust activity at day 100, as well as day 61; b) we added synapse quantification in Figure 4, and c) interneuron quantification in Figure 2. We are currently also pursuing high throughput measures of activity to assess the longitudinal activity of ACOs in a larger number of wells. This way we can more definitively quantify the time-dependent variance in organoid activity.

(5) Is this platform applicable to other functional measurements for neuronal activity, such as the MEA system? When observing the morphology of neurons formed in organoids, they appear to extend axons and dendrites in a consistent direction, suggesting a radial structure that demonstrates high reproducibility across wells. A culture system where neurons are arranged with such consistency in directionality could be highly beneficial for experiments utilizing the MEA system to assess parameters such as the speed of electrical activity transmission and stimulus-response. Therefore, there seems to be a need for a more detailed explanation of the utility of the structural characteristics of the culture system.

The ACO platform is indeed suitable for MEA recordings. We are in the process of engineering the required geometry using HD-MEA systems through specialized inserts to generate ACOs on MEA systems.

(6) In Figure 2E-I, authors suggest morphological diversity of GFAP+/S100b+ astrocyte, but the imaging data presented in Figure F-I is only based on GFAP immunoreactivity.

Since GFAP is also expressed in radial glial cells at this stage (Figure 2I), many fibrous astrocytes and interlaminar astrocytes are likely radial glial neural progenitor cells instead of astrocytes. It appears necessary to perform additional staining using astrocyte markers such as S100B or outer radial glia markers such as HOPX to demonstrate that the figure depicts subtype-specific morphologies of astrocytes.

In Figure 2M, we stained for GFAP and PAX6 to mark radial glia that look different than the astrocyte morphologies we describe in Figure 2J-L. We see a large overlap in GFAP and S100B staining in Figure 2I, in which most GFAP+ cells are double positive for S100B (yellow) that is more consistent with astrocyte maturation than radial glia. Furthermore, we have not seen PAX6 staining outside the dense edges of the center of the ACO.

(7) In Figure 4D, the axon appears to exhibit directionality. Additional explanation regarding the organization of the axon is necessary. Further research utilizing sparse staining to examine the morphology of single neurons seems warranted.

The polarized directionality of the axons is something we indeed have also noticed. We are looking into options to further investigate this intriguing property of the ACOs.

(8) Figure 1E-F only showed cell viability in the early stages around Day 40-50. To demonstrate the superior long-term viability of ACO culture, it appears necessary to illustrate the ratio of dead cells to live cells over the course of a time course.

Figure S1B shows LIVE/DEAD staining for ACOs of all three lines, revealing minimal DEAD staining at Day 56. A longitudinal time course experiment was not performed, however the line- and batch-specific quantifications over developmental timepoints in Figure S1C provide an indication of the robust long-term viability of the ACOs.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this fMRI study, the authors wished to assess neural mechanisms supporting flexible temporal construals. For this, human participants learned a story consisting of fifteen events. During fMRI, events were shown to them, and participants were instructed to consider the event from "an internal" or from "an external" perspective. The authors found distinct patterns of brain activity in the posterior parietal cortex (PPC) and anterior hippocampus for the internal and the external viewpoint. Specifically, activation in the posterior parietal cortex positively correlated with distance during the external-perspective task, but negatively during the internal-perspective task. The anterior hippocampus positively correlated with distance in both perspectives. The authors conclude that allocentric sequences are stored in the hippocampus, whereas egocentric sequences are supported by the parietal cortex.

We thank the reviewer for the accurate summary of our study.

Strengths:

The research topic is fascinating, and very few labs in the world are asking the question of how time is represented in the human brain. Working hypotheses have been recently formulated, and the work tackles them from the perspective of construals theory.

We appreciate the reviewer's positive and encouraging comments.

Weaknesses:

Although the work uses two distinct psychological tasks, the authors do not elaborate on the cognitive operationalization the tasks entail, nor the implication of the task design for the observed neural activation.

We thank the reviewer for bringing this issue to our attention. In the revised manuscript, we have added a paragraph to the Discussion acknowledging this potential limitation of the study. Please see our response below.

Reviewer #1 (Recommendations for the authors):

Overall, I thank the authors for providing clear responses and much-needed detail on their original work, which enables a better understanding of their perspectives. I still have some detailed questions about the reported work, which I provide below. It could help clarify the work for a more general audience and its replicability by the community.

We thank the reviewer for their positive evaluation of our previous revisions.

Main general concern:

I have one remaining core concern, which I distill as being a very different take on the usefulness of task design with neuroimaging. This concern follows from the authors' response to my original comment, which suggested possible confounds in fMRI data analysis and interpretation, as differences in task design and behavioral outcomes were not incorporated in the analytical approach.

The authors confirmed that "there is a substantial difference between the two tasks" but argue that these differences are not relevant seing that "the primary goal of this study was not to directly compare these tasks to isolate a specific cognitive component " However, the authors do perform such contrasts in their analysis (e.g. p. 10: "We first directly contrasted the activity level between external- and internal-perspective tasks in the time window of...") and build inferences on brain activation from them (e.g., p. 10: "Compared with the internal-perspective task, the externalperspective task specifically activated the...").

To clarify, my original concern was not about comparing neural activity in response to the two tasks but about the brain activity generated by two distinct tasks, which aim to reveal fundamentally distinct neural processes. The authors' response raises several concerns about the theoretical, methodological and empirical foundation of the work that are beyond the scope of a single empirical study and too long to detail here. Cognitive neuroscience relies on tasks to infer neural processes; this is the fertile and essential ground for using behavior in neuroscience to get to a mechanistic understanding of brain functions (e.g., Krakauer et al., 2017). In short, task design is fundamental because it shapes what neural processes are being investigated. Any inferences about brain activity recorded while a participant performs a task result from manipulated variables that should be under the control of the experimenter. Acknowledging that two tasks are distinct is acknowledging that different (neural) processes may govern their resolution. My initial remark was meant to highlight that, from basic signal detection theory, a same/different task and a temporal order task may not yield the same kind of basic biases and decision-making processes; these are far below and more basic than the posited sophisticated representations herein (construals, perspective taking).

In short, the general approach is far coarser than the level of interpretational granularity being pushed forward in the paper would suggest.

We greatly appreciate the reviewer’s comments and agree that this is a very fair point. We acknowledge that the two tasks differ in their underlying decision-making processes. In the revised manuscript, we have added a paragraph at the end of the Discussion to explicitly acknowledge this limitation and to outline possible avenues for future research (Page 23).

“One limitation of the present study is that the external- and internal-perspective tasks differed not only in the type of perspective-taking they were intended to elicit, but also in their underlying decision-making processes. The external-perspective task explicitly required participants to compare two events with respect to external temporal landmarks and judge whether they occurred in the same or different parts of the day (i.e., a same/different judgment), whereas the internalperspective task explicitly required participants to project themselves into a reference event and judge whether the target event occurred in the future or the past relative to that reference (i.e., a temporal-order judgment). This task design ensured that participants adopted two distinct perspectives on the event series, but at the expense of coherence in the cognitive operations required to make the two types of judgments. One alternative approach would be to more closely align the response demands of the two tasks by drawing on McTaggart’s (1908) A-series and Bseries distinction: in the external-perspective task, participants could judge whether the target event occurred before or after the reference event (i.e., a before/after judgment), whereas in the internal-perspective task they could judge whether the target event occurred in the past or future relative to the reference event (i.e., a past/future judgment). Although such a design would improve coherence in the underlying decision-making processes (i.e., both are temporal-order judgments), it would reduce experimental control over the perspective-taking manipulation. For example, before/after judgments could still be made from an internal perspective. Future studies are therefore needed to determine whether findings obtained from these two task designs converge.”

Additional clarifications:

Intro/theory

In this revised MS, the authors provided some clarifications of their theoretical perspective in the introduction. From my standpoint, the motivation remains insufficiently precise for a scientific report. Some theoretical aspects, such as construals or perspective taking remain evasive in relation to ego and allocentric representations. A couple of paragraphs dedicated to explaining what the authors mean precisely when using these terms would greatly help to situate the validity of the working hypothesis. In the absence of clear definitions, it remains difficult to evaluate what is being tested. For instance, what do the authors mean by "time construal"? How is a time construal the same or not as a "temporal distance" or a "temporal sequence"? This would greatly help the readership.

Additionally, some assertions are not clearly identified or fairly attributed. For instance, the assertion that EST provides a means to spatialize time is the authors' point of view or interpretation of this work, not an original proposition of the theory. Another example is McTaggart's metaphysics on time series (in the ontology of time in physics) "echoed" in linguistics; it has effectively been proposed and popularized by L. Boroditskty. The prospective and retrospective views of time should not be attributed to Tsao et al but to Hicks or Block in the 70's, who studied the psychology of time in humans.

We sincerely thank the reviewer for this criticism, which prompted us to clarify the relevant concepts in our manuscript. In the revised version, we made the following three main changes to the Introduction.

In the second paragraph of the Introduction (page 3), we clarify that event segmentation theory is independent of, but related to, the spatial construal of time hypothesis. We also clarify what we mean by time construals and explain that the two temporal components—duration and sequence—can be represented within such time construals, rather than constituting time construals themselves. These revisions were intended to prevent potential misunderstandings for the reader. In addition, we incorporated Boroditsky’s contributions relevant to this framework:

“One solution, which might be unique to humans, is to conceptualize time in terms of space (i.e., the spatial construal of time; e.g., Clark, 1973; Traugott, 1978; Lakoff & Johnson, 1980). Within this framework, time is usually first segmented into events—the basic temporal entities that observers conceive as having a beginning and an end (Zacks & Tversky, 2001). These temporal entities are then ordered in space, such that events occurring at different times can be maintained in working memory, allowing them to be flexibly accessed from different perspectives and easily referenced during communication (e.g., Casasanto & Boroditsky, 2008; Núñez & Cooperrider, 2013; Bender & Beller, 2014; Abrahamse et al., 2014; Figure 1A). The two core temporal components—duration and sequence—can be readily represented in such time construals.”

In the third paragraph of the Introduction (pages 3-4), we acknowledge the contributions of earlier behavioral studies on prospective and retrospective timing by citing the work suggested by the reviewer (Block & Zakay, 1997), which indicates that two distinct cognitive systems underlie timing processes. These behavioral findings converge with the conclusions of more recent neuroimaging studies:

“Unlike prospective timing tracking the continuous passage of time, durations in time construals are event-based (Sinha & Gärdenfors, 2014): the interval boundaries are constituted by events, and the event durations reflect their span (Figure 1A). Accumulating evidence suggests that distinct cognitive systems underlie these two types of duration (e.g., Block & Zakay, 1997). The motor and attentional system—particularly the supplementary motor area—has been associated with prospective timing (e.g., Protopapa et al., 2019; Nani et al., 2019; De Kock et al., 2021; Robbe, 2023), whereas the episodic memory system—particularly the hippocampus—is considered to support the representation of duration embedded within an event sequence (e.g., Barnett et al., 2014; Thavabalasingam et al., 2018; see also the comprehensive review by Lee et al., 2020).”

Block, R. A., & Zakay, D. (1997). Prospective and retrospective duration judgments: A meta-analytic review. Psychonomic Bulletin & Review, 4(2), 184-197.

In the fifth paragraph of the Introduction (page 5), we added a sentence to clarify the relationship between allocentric and egocentric reference frames and perspective taking:

“However, the neural mechanisms that enable the brain to generate distinct construals of an event sequence remain largely unknown. Valuable insights may be drawn from research in the spatial domain, which posits the existence of stable allocentric representations that are independent of viewpoint, from which variable egocentric representations corresponding to different perspectives can be generated.”

Methods:

While more detail is provided in the Methods, some additional detail would be helpful to enable the replication of this work. For instance,

- The table reports a sequence of phrases with assigned durations. Are the event phrases actual sentences given to participants? If so, how were participants made aware of the duration of the events, seeing that these sentence parts do not provide time information?

We apologize that we did not make this clear. The full text used during the reading phase of learning has already been provided in Figure 1—source data 1, which includes the information about event durations. In the revised manuscript, we now explicitly refer to this information in the Methods section (page 38): In the reading phase, participants read a narrative describing the whole ritual on a computer screen twice (Figure 1—source data 1).

- One of my original questions was about the narrative. In the Methods section, the authors state that participants read a text. Providing the full text would be helpful, also as a sanity check for sequentiality.

As clarified in the previous response, the texts are provided in Figure 1—source data 1, which illustrates the texts for both even- and odd-numbered participants.

- In the imagination phase, the authors introduce proportionality between imagination and experience (p. 37). What scale was used? What motivated it?

We thank the reviewer for bringing this issue to our attention. In this study, participants did not directly experience the events; instead, they learned the event information through narrative reading or imagination to ensure experimental control and efficiency. As clarified in the Methods section, the ratio between imagination duration and actual event duration was 30 seconds to 1 hour. In the revised manuscript, we have further explained our motivation for this design choice (page 39):

Here, we let participants learn the event information through narrative reading or imagination. Compared to learning through actual experience, this approach prioritizes experimental control and efficiency. The timing of the events is compressed, akin to the process of retrospectively recalling our experiences, in which we mentally traverse events without requiring the actual time they originally took. However, future studies may be needed to investigate whether the encoding of events from first- and second-hand experience differs.

Results:

- p. 10: the interpretation of the data on chunking and boundary effects should be properly referenced to e.g. Davachi's published work.

We thank the reviewer for highlighting Davachi’s important work on event boundaries. We have appropriately cited these studies in the revised manuscript (page 10), as reflected in the following passage: This pattern can be interpreted as a categorical effect: sequential distances within the same part of the day were perceived as shorter (i.e., a chunking effect), whereas distances spanning different parts of the day were perceived as longer (i.e., a boundary effect). Similar boundary- or chunking-related effects on event cognition have been reported in previous studies (e.g., Ezzyat & Davachi, 2011; DuBrow & Davachi, 2013; Radvansky & Zacks, 2017).

Ezzyat, Y., & Davachi, L. (2011). What constitutes an episode in episodic memory?. Psychological Science, 22(2), 243-252.

DuBrow, S., & Davachi, L. (2013). The influence of context boundaries on memory for the sequential order of events. Journal of Experimental Psychology: General, 142(4), 1277.

Radvansky, G. A., & Zacks, J. M. (2017). Event boundaries in memory and cognition. Current Opinion in Behavioral Sciences, 17, 133-140.

Reviewer #2 (Public review):

Summary:

Xu et al. used fMRI to examine the neural correlates associated with retrieving temporal information from an external compared to internal perspective ('mental time watching' vs. 'mental time travel'). Participants first learned a fictional religious ritual composed of 15 sequential events of varying durations. They were then scanned while they either (1) judged whether a target event happened in the same part of the day as a reference event (external condition); or (2) imagined themselves carrying out the reference event and judged whether the target event occurred in the past or will occur in the future (internal condition). Behavioural data suggested that the perspective manipulation was successful: RT was positively correlated with sequential distance in the external perspective task, while a negative correlation was observed between RT and sequential distance for the internal perspective task. Neurally, the two tasks activated different regions, with the external task associated with greater activity in the supplementary motor area and supramarginal gyrus, and the internal condition with greater activity in default mode network regions. Of particular interest, only a cluster in the posterior parietal cortex demonstrated a significant interaction between perspective and sequential distance, with increased activity in this region for longer sequential distances in the external task but increased activity for shorter sequential distances in the internal task. Only a main effect of sequential distance was observed in the hippocampus head, with activity being positively correlated with sequential distance in both tasks. No regions exhibited a significant interaction between perspective and duration, although there was a main effect of duration in the hippocampus body with greater activity for longer durations, which appeared to be driven by the internal perspective condition. On the basis of these findings, the authors suggest that the hippocampus may represent event sequences allocentrically, whereas the posterior parietal cortex may process event sequences egocentrically.

We sincerely appreciate the reviewers for providing an accurate, comprehensive, and objective summary of our study.

Strengths:

The topic of egocentric vs. allocentric processing has been relatively under-investigated with respect to time, having traditionally been studied in the domain of space. As such, the current study is timely and has the potential to be important for our understanding of how time is represented in the brain in the service of memory. The study is well thought out and the behavioural paradigm is, in my opinion, a creative approach to tackling the authors' research question. A particular strength is the implementation of an imagination phase for the participants while learning the fictional religious ritual. This moves the paradigm beyond semantic/schema learning and is probably the best approach besides asking the participants to arduously enact and learn the different events with their exact timings in person. Importantly, the behavioural data point towards successful manipulation of internal vs. external perspective in participants, which is critical for the interpretation of the fMRI data. The use of syllable length as a sanity check for RT analyses as well as neuroimaging analyses is also much appreciated.

We thank the reviewer for the positive and encouraging comments.

Suggestions:

The authors have done a commendable job addressing my previous comments. In particular, the additional analyses elucidating the potential contribution of boundary effects to the behavioural data, the impact of incorporating RT into the fMRI GLMs, and the differential contributions of RT and sequential distance to neural activity (i.e., in PPC) are valuable and strengthen the authors' interpretation of their findings.

My one remaining suggestion pertains to the potential contribution of boundary effects. While the new analyses suggest that the RT findings are driven by sequential distance and duration independent of a boundary effect (i.e., Same vs. Different factor), I'm wondering whether the same applies to the neural findings? In other words, have the authors run a GLM in which the Same vs. Different factor is incorporated alongside distance and duration?

We thank the reviewer for their positive evaluation of our previous revisions and are pleased that the additional analyses adequately address the boundary effects in the behavioral data and the RT effects in the neural data.

With respect to boundary effects in the neural data, we followed the reviewer’s suggestion and constructed a more complex GLM that incorporated the Same/Different part of the day as an additional regressors modulating the target events. Importantly, the same PPC region continued to show an interaction effect between Task Type and Sequential Distance. We have added this important control analysis in our revised manuscript (Pages 13–14):

“To further assess whether the observed PPC reactivation can be attributed to boundary or chunking effects introduced by the Parts of the Day, as well as other behavioral outputs, we performed an additional control analysis. Using a more complex first-level model, we included two extra regressors modulating the target events in both internal- and external-perspective tasks, alongside Sequential Distance and Duration: (1) Same/Different parts of the day (coded as 1/−1) and (2) Future/Past (coded as 1/−1). Even with these additional controls, the same PPC region remained the strongest area across the entire brain, showing an interaction effect between Task Type and Sequential Distance, although the cluster size was slightly reduced (voxel-level p < 0.001; clusterlevel FWE-corrected p = 0.054).”

Reviewer #2 (Public review):

Summary:

The manuscript by Selvaratnam et al. defines how the transcription factor HEB integrates with TCR signaling to regulate Id3 expression in the context of gdT17 maturation in the fetal thymus. Using conditional HEB ablation driven by Vav Cre, flow cytometry, scRNA-seq, and reanalysis of ChIP-seq data the authors, provide evidence for a sequential model in which HEB and TCR-induced Egr2 cooperatively upregulate Id3, enabling gdT17 maturation and limiting diversion to the ab lineages. The work provides an important mechanistic insight into how the E/ID-protein axis coordinates gd T cell specification and effector maturation.

Strengths include:

(1) The proposed model that HEB primes, TCR induces, and Id3 stabilizes gdT17 cells in embryonal development is elegant and consistent with the findings.

(2) The choice of animal models and the study of a precise developmental window.

(3) The cross-validation of flow, scRNA-seq, and ChIP-seq reanalyses strengthens the conclusions.

(4) The study clarifies the dual role of Id3, first as an HEB-dependent maturation factor for gdT17 cells, and as a suppressor of diversion to the ab lineages.

Comments on revisions:

In this revised version of their manuscript the authors have effectively addressed all of my previous concerns. In its current form the study represents a significant advancement in our understanding of how the transcription factor HEB integrates with TCR signaling to regulate Id3 expression in the context of gdT17 maturation in the fetal thymus. In this revised version of their manuscript the authors have effectively addressed all of my previous concerns. In its current form the study represents a significant advancement in our understanding of how the transcription factor HEB integrates with TCR signaling to regulate Id3 expression in the context of gdT17 maturation in the fetal thymus.

Author response:

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

We thank the reviewers for their enthusiasm and insightful suggestions. Our responses to specific concerns and questions are detailed below.

Public Reviews:

Reviewer #1 (Public review):

The authors use Flow cytometry and scRNA seq to identify and characterize the defect in gdT17 cell development from HEB f/f, Vav-icre (HEB cKO), and Id3 germline-deficient mice. HEB cKO mice showed defects in the gdT17 program at an early stage, and failed to properly upregulate expression of Id3 along with other genes downstream of TCR signaling. Id3KO mice showed a later defect in maturation. The results together indicate HEB and Id3 act sequentially during gdT17 development. The authors further showed that HEB and TCR signaling synergize to upregulate Id3 expression in the Scid-adh DN3-like T cell line. Analysis of previously published Chi-seq data revealed binding of HEB (and Egr2) at overlapping regulatory regions near Id3 in DN3 cells.

The study provides insight into mechanisms by which HEB and Id3 act to mediate gdT17 specification and maturation. The work is well performed and clearly presented. We only have minor comments.

Reviewer #2 (Public review):

Summary:

The manuscript by Selvaratnam et al. defines how the transcription factor HEB integrates with TCR signaling to regulate Id3 expression in the context of gdT17 maturation in the fetal thymus. Using conditional HEB ablation driven by Vav Cre, flow cytometry, scRNA-seq, and reanalysis of ChIP-seq data the authors, provide evidence for a sequential model in which HEB and TCR-induced Egr2 cooperatively upregulate Id3, enabling gdT17 maturation and limiting diversion to the ab lineages. The work provides an important mechanistic insight into how the E/ID-protein axis coordinates gd T cell specification and effector maturation.

Strengths include:

(1) The proposed model that HEB primes, TCR induces, and Id3 stabilizes gdT17 cells in embryonal development is elegant and consistent with the findings.

(2) The choice of animal models and the study of a precise developmental window.

(3) The cross-validation of flow, scRNA-seq, and ChIP-seq reanalyses strengthens the conclusions.

(4) The study clarifies the dual role of Id3, first as an HEB-dependent maturation factor for gdT17 cells, and as a suppressor of diversion to the ab lineages.

Weaknesses:

(1) The ChIP-seq reanalysis indicates overlapping HEB, E2A, and Egr2 peaks ~60 kb upstream of Id3. Given that the Egr2 data are not generated using the same thymocyte subsets, some form of validation should be considered for the co-binding of HEB and Egr2, potentially ChIP-qPCR in sorted gdT17 progenitors.

We agree that this is a valid concern and continue to work on confirming the mechanism from several other angles. Validating HEB/E2A and Egr2 co-binding in gdT17 cell progenitors by ChIP-qPCR would/will be a very precise and definitive experiment, but it will be very challenging to perform, in part due to the low numbers of gdT17 precursors in the fetal thymus (note the y-axis scales in Fig. 1F, J). As a complementary approach, we have analyzed additional ChIP-seq data for HEB/E2A binding in Rag2^-/- DN3 cells retrovirally transduced with the KN6 gdTCR cultured with stroma expressing the weak KN6 ligand T10 for 4 days. This analysis revealed that the binding of HEB/E2A on those sites persisted after weak gdTCR signaling, strengthening the likelihood that concurrent binding of HEB/E2A and Egr2 occurs during this developmental transition. We noted that HEB/E2A binding was slightly dampened in Rag2^-/- DN3 + gdTCR cells relative to Rag2^-/- DN3 cells, consistent with the induction of Id3 and subsequent Id3-mediated disruption of E protein binding. We also located HEB/E2A and Egr binding sites in close proximity in the two regions that shared peaks between HEB/E2A and Egr2 analyses (HE1 and HE2), in line with the potential participation of these two transcription factors in an enhanceosome binding complex.

Furthermore, we examined the chromatin landscape of the Id3 locus by sorting WT DN3 and DN4 cells, as well as Rag2^-/- DN3 cells to provide a genuine pre-selection context, and performing ATAC-seq (Figure 7–suppl 7A). Given the known ability of E2A and HEB to induce chromatin remodeling, we also examined accessibility in DN3 and DN4 cells from HEB cKO mice. Alignment of ATAC-seq and ChIP-seq peaks in the Id3 locus revealed accessibility of HE1 and HE2 in Rag2^-/-, WT DN3, and WT DN4 cells. However, accessibility of HE1 and HE2 was dampened in HEB cKO cells, especially at the DN3 stage, suggesting that HEB may be involved in remodeling the Id3 locus, resulting in a poised state that enables TCR-dependent transcription factors to induce Id3 proportionally to TCR signal strength. These data are now presented as a new “Figure 7 – figure supplement 1” with corresponding Results, Discussion, and Methods updates.

Our next story will be focused on a finer dissection of the Id3 cis-regulatory elements and their combinatorial regulation by HEB/E2A and other transcription factors, and how they relate to specific signaling pathways. For this study, we will modify the language regarding Egr2 to reflect the open questions that still remain to be addressed.

(2) E2A expression is not affected in HEB-deficient cells, raising the question of partial compensation, a point that should be specifically discussed.

This confounding factor is always an issue with E proteins. We have now added a section to the discussion that highlights previous literature and relates it to our findings.

(3) All experiments are done at E18, when fetal gdT17 development predominates. The discussion could address whether these mechanisms extend to neonatal or adult gdT17 subsets.

In our 2017 paper (PMID 29222418) we showed that HEB cKO mice have defects in the production of functional gdT17 cells in fetal and neonatal thymus and in the adult periphery (in lungs and spleen). While the adult thymus does not support the development of fully functional innate gd T cells, it does contain gdTCR+ cells that have activated the Sox-Maf-Rorc network (Yang 2023, PMID 37815917). It will be very interesting to assess the impact of HEB loss on these cells, and we are actively pursuing this goal. For now, we will add a paragraph to the discussion addressing what we know from previous work and what is yet to be learned.

Reviewer #3 (Public review):

Summary:

The authors of this manuscript have addressed a key concept in T cell development: how early thymus gd T cell subsets are specified and the elements that govern gd T17 versus other gd T cell subsets or ab T cell subsets are specified. They show that the transcriptional regulator HEB/Tcf12 plays a critical role in specifying the gd T17 lineage and, intriguingly, that it upregulates the inhibitor Id3, which is later required for further gd T17 maturation.

Strengths:

The conclusions drawn by the authors are amply supported by a detailed analysis of various stages of T cell maturation in WT and KO mouse strains at the single cell level, both phenotypically, by flow cytometry for various diagnostic surface markers, and transcriptionally, by single cell sequencing. Their conclusions are balanced and well supported by the data and citations of previous literature.

Weaknesses:

I actually found this work to be quite comprehensive. I have a few suggestions for additional analyses the authors could explore that are unrelated to the predominant conclusions of the manuscript, but I failed to find major flaws in the current work.

I note that HEB is expressed in many hematopoietic lineages from the earliest progenitors and throughout T cell development. It is also noteworthy that abortive gamma and delta TCR rearrangements have been observed in early NK cells and ILCs, suggesting that, particularly in early thymic development, specification of these lineages may have lower fidelity. It might prove interesting to see whether their single-cell sequencing or flow data reveal changes in the frequency of these other T-cell-related lineages. Is it possible that HEB is playing a role not only in the fidelity of gdT17 cell specification, but also perhaps in the separation of T cells from NK cells and ILCs or the frequency of DN1, DN2, and DN3 cells? Perhaps their single-cell sequencing data or flow analyses could examine the frequency of these cells? That minor caveat aside, I find this to be an extremely exciting body of work.

Excellent question, and the underlying answer is yes, loss of HEB renders the cells more open to divergence to non-T lineages, even at the DN3 stage. Although our datasets did not reveal those cells, we have examined this question previously. In our 2011 paper (Braunstein, 2011, PMID 21189289) where we identified “DN1-like” cells arising from HEB-/- DN3 cells in OP9-DL1 co-cultures. These cells responded to IL-15 and IL-7 by differentiating into cytotoxic NK-like cells. We did not detect TCRb rearrangements but did not look for gdTCR rearrangements. Subsequently, multiple papers from other labs showed that ILC2 were greatly expanded in the thymus using Id-overexpression transgenic mice and HEB/E2A-double deficient mice (Miyazaki, 2023, PMID 28514688; Miyazaki, 2025, PMID 39904558; Berrett, 2019, PMID 31852728; Qian, 2019, PMID 30898894; Peng, 2020, PMID:32817168). The ILCs in these mice had TCRg rearrangements, consistent with a shared origin with WT thymic-derived ILCs. In unpublished data from our lab, we found an increase in the numbers of ILC2 but not ILC3 in HEB cKO fetal thymic organ cultures. We did not follow up on this work any further since the topic was being heavily pursued in other labs, but remain very interested in this branchpoint, and will mention the literature in the discussion.

Joint recommendations for the authors:

(1) Experimental validation (for mechanistic clarity)

The ChIP-seq reanalysis indicates overlapping HEB, E2A, and Egr2 peaks ~60 kb upstream of Id3. Given that the Egr2 data are not generated using the same thymocyte subsets, some form of validation should be considered for the co-binding of HEB and Egr2, potentially ChIP-qPCR in sorted gdT17 progenitors to substantiate the proposed cooperative mechanism.

See above; new experiments with ATAC-seq and additional ChIP-seq analysis.

(2) Figures

Potential inconsistencies in Figure 1H: In the legend to Figure 1H, Vg1-Vg5- cells are considered Vg6+ cells. Flow plots show reduced A Vg1-Vg5- population in HEBc ko mice, but the accompanying bar plot shows increased frequency of Vg6+ cells.

Vg6 cells are actually considered to be Vg4-Vg5-Vg1- cells (not Vg4- Vg1- cells, which is important in the fetal context). The flow plot shows the percentage of Vg6 cells out of the Vg1-Vg4- population, whereas the bar plot shows the percentage of Vg6 cells out of all gdTCR+ cells. The ratio of Vg6 to Vg5 cells decreases within the Vg1-Vg4- population, whereas the overall percentages and numbers of Vg6 cells in all gd T cells is increased in HEB cKO mice. We have now more clearly explained this in the text and the figure legend.

Clarify which cells produce IL-17A in Figure 1L.

This plot is gated on all gd T cells stimulated with PMA/ionomycin; this has been added to the results and figure legend.

In Supplementary Figure 2, legend, do the authors mean that TRGV4 was depleted? The authors write TRDV4. Please check.

Thank you for catching this mistake, we have corrected it.

In Figure 7, the Author showed Id3 mRNA expression. Can the expression of Id2 be included?

That is a really interesting question, and we will follow up on it in future studies.

If Id1 or Id4 are relevant for any of these studies, can their expression be shown in Supplementary Figure 3A? If these are minimally expressed or not expressed, this could be mentioned.

Id1 and Id4 were not detectable in our studies, this is now stated in the results section describing expression of E proteins and Id proteins.

(3) Discussion

Discuss possible redundancy between HEB and E2A, as E2A expression appears unaffected in HEB-deficient cells.

See above

Address whether the mechanisms identified at E18 (embryonic stage) also apply to neonatal or adult γδT17 subsets.

See above

Expand on how HEB function may relate to other hematopoietic or early lymphoid lineages (NK/ILC, DN1-DN3 stages), based on reviewer curiosity.

See above

(4) Methods and terminology

Define the terms γδTe1 and γδTe2 (e.g., early effector subsets).

This has been defined more clearly in several sections of the text.

Add details to the scRNA-seq methods section (average number of cells analyzed and sequencing depth per cell).

These details have been added.

Author response:

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

We now performed new experiments that were included in the manuscript. Our new results show that that monocyte-derived dendritic cells primed in vivo during P. chabaudi infection, or in vitro with TNF express high levels or GLUT-1 (Figures 4M, 5D, 6L). Furthermore, our new data show that mice treated with 2-DG (na inhibitor of glycolysis) are more susceptible to infection (Figures 6N, O). In addition, new results of glucose uptake by muscle and adipose tissues were added to the manuscript. Finally, figure legends were revised, densitometric analysis performed, and other issues addressed in the text.

Please see below a point-by-point reply to the Reviewers’ comments.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The manuscript by Kely C. Matteucci et al. titled "Reprogramming of host energy metabolism mediated by the TNF-iNOS-HIF-1α axis plays a key role in host resistance to Plasmodium infection" describes that TNF induces HIF-1α stabilization that increases GLUT1 expression as well as glycolytic metabolism in monocytic and splenic CD11b+ cells in P. chabaudi infected mice. Also, TNF signaling plays a crucial role in host energy metabolism, controlling parasitemia, and regulating the clinical symptoms in experimental malaria.

This paper involves an incredible amount of work, and the authors have done an exciting study addressing the TNF-iNOS-HIF-1α axis as a critical role in host immune defense during Plasmodium infection.

Reviewer #2 (Public Review):

Summary:

The premise of the manuscript by Matteucci et al. is interesting and elaborates on a mechanism via which TNFa regulates monocyte activation and metabolism to promote murine survival during Plasmodium infection. The authors show that TNF signaling (via an unknown mechanism) induces nitrite synthesis, which (via yet an unknown mechanism), and stabilizes the transcription factor HIF1a. Furthermore, HIF1a (via an unknown mechanism) increases GLUT1 expression and increases glycolysis in monocytes. The authors demonstrate that this metabolic rewiring towards increased glycolysis in a subset of monocytes is necessary for monocyte activation including cytokine secretion, and parasite control.

Strengths:

The authors provide elegant in vivo experiments to characterize metabolic consequences of Plasmodium infection, and isolate cell populations whose metabolic state is regulated downstream of TNFa. Furthermore, the authors tie together several interesting observations to propose an interesting model.

Weaknesses:

The main conclusion of this work - that "Reprogramming of host energy metabolism mediated by the TNF-iNOS-HIF1a axis plays a key role in host resistance to Plasmodium infection" is unsubstantiated. The authors show that TNFa induces GLUT1 in monocytes, but never show a direct role for GLUT1 or glucose uptake in monocytes in host resistance to infection (nor the hypoglycemia phenotype they describe).

We kindly disagree with the Reviewer. There is a series of experiments showing that TNFR KO (Figures 1, 2, 4), HIF1a KO (Figure 5) and iNOS KO (Figure 6) mice have partially impaired inflammatory response and control of parasitemia (Figures Figures 1E, 5G and 6B).

To further address the issue raised by the reviewer, we performed two sets of experiments. First, we show, in vitro, the impact of TNF stimulation on GLUT1 expression and glucose uptake (Figure 4M, 5D, 6L). Our results show that GLUT1 is increased after 18 hours with TNF (100 ng/mL) stimulation in MODCs from WT mice but not from iNOS KO, HIF1a KO e TNFR KO mice. Similar results were obtained with monocytic cells derived from infected mice (Figure 4L, 5C, 6K). The results support the discussion by demonstrating that TNF stimulation influences GLUT1 expression in monocytic cells. This aligns with the proposed mechanism that TNF signaling regulates HIF-1α stabilization and glycolytic metabolism via RNI. The absence of GLUT1 upregulation and glucose uptake in TNFR KO, iNOS KO and HIF-1α KO mice further reinforces the role of RNI in promoting HIF-1α stabilization, as suggested in the discussion.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Major points

All Figure legends are not precise about the data express means {plus minus} standard errors of the means (SEM) or SD. Figure 1D shows no SD in the data from the uninfected group. It strongly suggests precise and improving all figure legends, giving more details in terms of including an explanation of all symbols, non-standard abbreviations, error bars (standard deviation or standard error), experimental and biological replicates, and the number of animals, and representative of the independent experiments.

We apologize for the lack of details in the Figure legends. As requested, we are now indicating whether we used SEM or STDV, number of mice per group, number of replicate experiments. We also clarified the groups that are being compared, and the statistical significance indicated by the symbols. We also standardized symbols as asterisk only, and number of asterisk indicating the significance.

Figure 1. The figure legend has no information about the organ for which TNF mRNA was measured (Figure 1D). Also, regarding the TNF data, Figure 1 C e 1D shows that the circulating levels of TNF and the expression of TNF mRNA in the liver peaked at the same time point, and after 6h, there is no difference between infected and uninfected mice. It would be expected that the TNF mRNA expression would be detected earlier than the protein, assuming that the primary source of TNF is from the liver. Is there another organ that could mainly source blood TNF levels? Did the authors have a chance to measure the blood TNF levels during infection (0-8dpi), besides the measurement at different times only on day 8?

We included in the legend of Figure 1D that mRNA was extracted from liver.

Liver and spleen are the main reservoir of infected erythrocytes and the main source of cytokines during the infection with the erythrocytic stage of malaria. The results presented in Figures 1C and 1D are from in vivo experiments, not a controlled cellular experiment in vitro. So, we can not conclude about exact time and synchronous production of TNF mRNA and protein. We have published earlier that during P. chabaudi infection, the peaks of TNF mRNA expression and the levels of circulating TNF protein occur between midnight and 6 am (Hirako at al., 2018). Hence the results are consistent in the results described here. In addition, this earlier study also shows that the same pattern of TNF at days 6 and 8 post-infection are similar. Furthermore, in another studies, we reported that the peak of TNF production occurs between days 6 and 10 post P. chabaudi infection (Franklin et al, PNAS, 2009; Franklin et al, Microbes and Infection, 2007). This is now clarified in the text (page 05, line 132):

“As previously demonstrated, the circulating levels of TNF and expression of TNF mRNA in the liver peaked at 6 am (end of dark cycle) at 8 dpi (Figure 1C and 1D), and has been reported to peak between days 6 and 10 post-infection, with a consistent pattern observed on days 6 and 8.”

Figure 2. "We observed that in naïve animals, all of these parameters were similar in TNFR^-/- and C57BL/6 mice (Figures 2A-D, top panels, and Figures 2E-H)." Interestingly, the respiratory exchange rate of TNFR^-/- uninfected mice seems higher in TNFR^-/- uninfected mice than in naïve uninfected mice, and this pattern seems to be more pronounced in TNFR^-/- uninfected mice. Is there any suggestion that could explain the change in respiratory exchange rate behavior without infection in those animals?

At the moment, we have not investigated the basis of this difference between uninfected WT and TNFR KO mice, which goes beyond the scope of this research. This is indeed an interesting observation that should be pursued in the future by our group and elsewhere. We mentioned this difference, when describing the results (page 06, lines 155):

“We observed that in naïve animals, all of these parameters were similar in TNFR^-/- and C57BL/6 mice (Figures 2A-D, top panels and Figures 2E-H), with a slightly higher respiratory exchange rate in uninfected TNFR^-/- mice. In contrast, all the evaluated parameters were decreased in infected C57BL/6 mice compared to their naïve counterparts during the light and dark cycles. When we analyzed only infected mice, the alterations in all parameters were milder in TNFR^-/- compared to C57BL/6 mice (Figures 2A-D bottom panels and 2E-H).”

Figure 3. To give an idea of the main population of non-parenchymal cells, it will be helpful to clarify briefly how non-parenchymal cells from the liver of infected or uninfected mice were isolated.

We described in detail at Material and Methods (Page 19, Lines 566.)

Figure 3, B, C, D, G and Figure 4K and Figure 5 A and B - Semi-quantitative data through the densitometric analysis of western blots should be included in all figures.

Thank you for the suggestion. We now included the densitometric analysis for all Western blot results in Supplementary figure.

Figure 4. The author describes, "We observed that except for Hexokinase-3, the expression of mRNAs of glycolytic enzymes (Hexokinase-1, PFKP, and PKM) was increased in C57BL/6 but not TNFR-/- 8dpi." Sometimes, it is hard to understand which groups have been compared to some data. Be precise in describing the statistical analysis between the groups. It seems that those genes were increased in "infected C57BL/6 in comparison to uninfected mice, but not TNFR-/- 8-dpi. Moreover, even though the authors include statistic symbols "ι, ιι, ιιι" in other legends, there is no explanation about statistic symbols in the legend of Figure 4.

As mentioned above, we improved the descriptions of all figures in the legend, and when necessary in the main text describing the results.

Figure 5. The authors describe, "We found that GLUT1 protein and glycolysis (ECAR) was impaired, respectively, in monocytic cells and splenic CD11b+ cells from infected, as compared to uninfected HIF-1aΔLyz2 mice (Figures 5C-5E)." The GLUT-1 expression was inhibited in both cells compared to HIF-1afl/fl mice but not even close to impaired GLUT-1 expression. There is still a robust amount of GLUT-1 expression, and significantly higher when compared to cells from uninfected mice.

We tuned our statement to partially impaired, indicating that other host or parasite components maybe be also influencing GLUT-1 expression. In fact, we have recently published that IFNγ has also an important role in regulating GLUT1 expression in MO-DCs and this reference is mentioned in the text (page 10, line 291):

“We found that glycolysis (ECAR) and GLUT1 expression were impaired, though partially, in monocytic and splenic CD11b+ cells from infected HIF-1aΔLyz2 mice (Figures 5C-5E) compared to infected WT mice. The level of GLUT1 expression that is still maintained is likely due to other host or parasite factors, such as IFN-γ (Ramalho 2024).”

Figure 6. It is essential to have more information about the number of replicates in Figure 6A. However, there are just two dots replicates in the condition CD11b+ splenic cells from C57BL/6 stimulated with or without LPS (purple bars). It is essential to be precise regarding the number of experimental and biological replicates in each experiment and the statistical analysis that has been applied, including this group. Furthermore, the author concludes, "...these data demonstrated that RNI induces HIF-1α expression...." This conclusion needs a more careful description since no data supports that monocytic cells or splenic CD11b+ cells from iNOS-/- infected mice decrease stabilization of HIF-1αm using blotting, as shown in Figure 5 A.

As mentioned above the number of replicates for each experiment was included in the figure legends.

Minor Points.

Figure 3. "Hepatocytes have an important role in glucose uptake from the circulation, and they do this primarily through GLUT2 (38), whose mRNA expression was downregulated (Figure 3A) and protein expression unchanged in response to Pc infection (Figure 4K)." I suggest moving the Figure 4K to Figure 3 to make it easy to follow the data description.

We thank the reviewer for the suggestion. However, we chose to keep Figure 4K in Figure 4, as this panel includes data from TNF receptor deficient mice, and the analysis of TNF knockout models is first introduced and discussed in Figure 4. For clarity and consistency, we therefore maintained this panel within Figure 4.

Line 433. Replace iNOS for iNOS-/- mice.

iNOS is now replaced for iNOS-/- mice.

Reviewer #2 (Recommendations For The Authors):

The premise of the manuscript by Matteucci et al. is interesting and elaborates on a mechanism via which TNFa regulates monocyte activation and metabolism to promote murine survival during Plasmodium infection. The authors show that TNF signaling (via an unknown mechanism) induces nitrite synthesis, which (via yet an unknown mechanism), and stabilizes the transcription factor HIF1a. Furthermore, HIF1a (via an unknown mechanism) increases GLUT1 expression and increases glycolysis in monocytes. The authors demonstrate that this metabolic rewiring towards increased glycolysis in a subset of monocytes is necessary for monocyte activation including cytokine secretion, and parasite control.

The main goal of this work is to study the interplay of TNF/HIF1a/iNOs in the pathogenesis in an experimental model of malaria. To dissect the molecular mechanism by which TNF induces reactive nitrogen species and regulates HIFa expression is beyond the scope of our research. Nevertheless, there is a vast literature addressing these issues. We now include in the discussion a paragraph describing the main conclusion of these studies published previously (page 12, line 363):

"Previous studies have shown that TNF induces the production of RNI through the upregulation of iNOS via the NF-κB pathway (63, 64). TNF-mediated iNOS expression is critical for NO production, which in turn stabilizes HIF-1α by inhibiting prolyl hydroxylases (PHDs) even under normoxic conditions (58, 59). HIF-1α then upregulates the expression of glycolytic genes, including GLUT1 (22, 62).”

Major comments

Issues concerning novelty

Some of the reported observations are not novel. TNFa and TNFa signaling has been demonstrated to contribute to the release of certain cytokines, and to contribute to the control parasitemia (PMID: 10225939). TNFa has been shown to increase glucose uptake in tissues (PMID: 2589544). There is a textbook about the role of INOS during the pathogenesis of malaria, including its association with parasite control (https://link.springer.com/chapter/10.1007/0-306-46816-6_15). Furthermore, other mechanisms controlling glycemia during Plasmodium infection have been shown (PMID: 35841892). The authors should adequately discuss other papers which have reported some of their findings.

Thanks for the comments on previously existing literature. We are well aware of some of this earlier literature. Some of these earlier findings are mentioned in our manuscript. We emphasized these fundamental findings in the discussion, as requested (page 12, line 368):

“TNF has been described as a critical mediator in malaria, driving cytokine release and parasitemia control (PMID: 10225939). It also enhances glucose uptake in tissues, aligning with our findings of increased glycolysis in monocytes (PMID: 2589544). The role of iNOS in malaria is well documented. IFN-γ and TNF induced the production of NO, which inhibits parasite growth but can cause tissue damage and organ dysfunction, especially in severe malaria (Mordmüller et al., 2002). Recent studies also highlight the complexity of glycemia regulation during Plasmodium infection describing its role in modulating parasite virulence and transmission (PMID:35841892). These studies demonstrate the critical function of TNF and iNOS in immune responses against Plasmodium, aligning with our findings of this axis and metabolic rewiring that are essential for monocyte activation and outcome of Pc infection.”

The authors claim that "Reprogramming of host energy metabolism mediated by the TNF-iNOS-HIF1a axis plays a key role in host resistance to Plasmodium infection," and contributes significantly to their effector functions (particularly parasite clearing), and the systemic drop in glycemia observed during Pc infection. Although the authors show that TNFa does result in altered metabolism and increased GLUT1 levels in a subpopulation of monocytes, the evidence that TNFa-induced glylcolysis plays a key role in host resistance is correlative at best.

This is an important question. We did show that TNFR KO have higher parasitemia. But TNF is pleiotropic cytokine and has multiple roles on innate and acquired immunity. The experiment we have performed and helps to address this issue is the in vivo treatment with 2DG. We found that treatment with this inhibitor of glycolysis results in a increase of parasitemia. These results are now included in Figure 6.

When considering that the majority of monocytic populations are reduced in frequency and only a small subset (i.e., Monocyte-derived DCs) increase in frequency (Fig 3K) during Pc infection, this makes it very difficult to demonstrate that a cell population whose overall frequency reduces contributes significantly to the drop in glycemia during Pc infection. The authors should therefore include experiments that demonstrate that the inhibition of glycolysis induced by TNFa in monocytes is protective and/or contributes to a decrease in extracellular glucose. The authors could assess the impact of the loss of function of GLUT1 on activated monocytes and monocyte-derived DCs on glycemia upon TNFa stimulation.

We agree. We focused on monocytes and the derived inflammatory monocytes and MO-DCs. In fact, the frequency of monocytes, considering the inflammatory monocytes and MO-DCs, is increased both in spleen and liver. One interesting result is that the HIF1a Lysm KO mice has impaired metabolism, attenuated hypoglycemia and increased parasitemia (Figure 5). Nevertheless, we agree that our current data thus not proof that the glycemia is due to the consumption of glucose by the activated monocytes, and that these are the only cells with increased glucose consumption. This is now added to the discussion (page 13, line 395):

"Although the frequency of MO-DCs increases during infection, other cell populations may also contribute to glucose consumption. Further experiments, including the assessment of GLUT1 function in these populations, are needed to clarify their contribution to glucose consumption during infection."

Furthermore, in the current state of the manuscript, it is unclear how activated monocyte populations uptake glucose. The authors claim that glucose uptake by activated monocytes is GLUT1-dependent, however, glucose transport via GLUT1 is insulin-dependent. Since Plasmodium infection is associated with insulin resistance, and almost unquantifiable levels of insulin (PMID: 35841892), and TNFa itself induces insulin resistance (PMCID: PMC43887), it is unclear how the activated monocyte population uptakes glucose. If the authors consider TNFa to be sufficient for GLUT1 induction, in vitro experiments (TNFa+monocytes) could bolster this claim (and support that GLUT1 is induced in an insulin-independent mechanism.

There is significant evidences indicating that in contrast to GLUT4, induction of GLUT1 in mice is independent of insulin (PMID: 9801136). In our case, seems to be induced by the cytokines TNF and IFN𝛾(this study and Ramalho et al., 2024). We now performed experiments exposing monocytes to TNF and evaluating GLUT1 expression. The results indicate that monocytes exposed to TNF (100 ng/mL) for 18 hours from WT mice exhibited a significant increase in GLUT1 expression. This increase was comparable to the increased-GLUT1 phenotype observed in infected animals. The results of this experiment were included in the manuscript.

A text was included to the discussion to clarify the issue of insulin dependence of GLUT1 expression (page 13, line 388):

“GLUT1 expression is recognized as independent of insulin, in contrast to GLUT4 (PMID: 9801136). In our model, this regulation appears to be driven by pro-inflammatory cytokines, particularly TNF. Supporting this, our results show that in vitro stimulation with TNF, significantly increases GLUT1 expression in monocytes, accordingly to the ex vivo phenotype observed in infected animals.”

Alternative hypothesis which might explain their phenotypes

Figure 2 A-H: The metabolic effects of the genetic manipulations including INOS KO, TNFR KO, and HIF-1α∆Lyz2 could be explained by lesser disease morbidity owed to a reduction of inflammatory response during infection. Under this condition, the development of anorexia will not be as profound in the knock-outs compared with wild-type littermate controls, since anorexia of infection is tightly linked to the magnitude of inflammatory response. Accordingly, infected knock-out animals can keep eating, which presumably impacts glycemia, maintenance of core body temperature, and overall energetics of infected mice. The authors should exclude this possibility.

We consider this possibility and the discussion now elaborates about this alternative hypothesis. We believe, that these two mechanisms are not mutually exclusive (page 16, line 474):

“Although restored physical activity, food consumption and energy expenditure in knockout mice may contribute to the observed systemic metabolic parameters by altering energy balance, these effects are not mutually exclusive with the TNF-driven, cell-intrinsic metabolic mechanisms described here.”

Minor comments

The authors showed increased parasitemia upon TNFR and HIF1a depletion in the LyZ2 compartment. The same was observed upon organismal INOS depletion. This raises the question of whether the TNFHIF-INOS signaling axis is adaptive or maladaptive during Pcc infection. The authors should show host survival in mice lacking TNFR and HIF1a in the LyZ2 compartment, and in mice lacking INOS (presumably, they have these data).

Despite the fact the various knockout mice have increased parasitemia and signs of disease, they all survive the infection. This is now included in the Figure legends.

Are the higher tissue glucose levels specific to the liver and the spleen or this is a more general event? Have the authors looked at other organs?

We now added the results of glucose uptake in the muscle and adipose tissues in figure 2. The fact that the glucose uptake is not increased in muscle and adipose tissue, further suggest that the increased glucose uptake in this model is insulin independent.

Figure 1F: All core body temperatures are within the physiological range, i.e., >36 degrees C. This makes it unclear why the authors regarded this as hypothermia. The authors should present experiments demonstrating the development of hypothermia in Figure 1F, as they claim this.

Temperature changes in mouse kept in animal house have been an issue discussed in the field. It is clear, however, that early in the morning (end of active period) mice have torpor. Lower temperature and physical activity.

In Figure 4, since the authors already suggested that extra-hepatic cells, and not the liver parenchyma, contribute to glucose uptake, the authors should clarify why they analyzed the whole liver in Figure 4, and not extra-hepatic cells. Furthermore, the authors should quantify the hepatic monocytic population in non-infected versus infected wild-type animals.

The reason we used whole liver, is that the number of non-parenchymal cells obtained from liver is limited for Western blot analysis. We thought that was important to show that expression of GLUT1 was decreased in the liver of TNFR KO mice. Nevertheless, the level of TNFR expression in different cell types in the liver was shown by flow cytometry. In addition, we performed the WB with cells extracted from the spleen, where lymphoid and myeloid cells are more abundant.

Line 87: Phagocytizing parasitized what?

This has been corrected in the manuscript.

Line 111 Define RNI before being used.

Is there a gender disparity in the TNFR KO phenotype? If yes, the authors should comment about this in their discussion.

This has been defined and addressed in the manuscript

Line 192: Did the authors mean 3B??

In 3M, please plot monocytes from uninfected animals.

The plot of uninfected animals are now included in Figure 3M

Line 390 Remove the extra dash in HIF1a.

Extra dash has been removed.

Line 397 Define RA

RA is now defined.

Author response:

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

eLife Assessment

This study represents an important advance in our understanding of how certain inhibitors affect the behavior of voltage gated potassium channels. Robust molecular dynamics simulation and analysis methods lead to a new proposed inhibition mechanism with strength of support being mostly convincing, and incomplete in some aspects. This study has considerable significance for the fields of ion channel physiology and pharmacology and could aid in development of selective inhibitors for protein targets 

We are encouraged by this favorable assessment and thank editors and reviewers for their constructive feedback and recommendations. We trust that the revisions made to the manuscript will clarify the aspects that had been perceived to be incomplete.

Reviewer #1 (Public review):

Summary: 

This study seeks to identify a molecular mechanism whereby the small molecule RY785 selectively inhibits Kv2.1 channels. Specifically, it sought to explain some of the functional differences that RY785 exhibits in experimental electrophysiology experiments as compared to other Kv inhibitors, namely the charged and non-specific inhibitor tetraethylammonium (TEA). This study used a recently published cryo-EM Kv2.1 channel structure in the open activated state and performed a series of multi-microsecond-long all-atom molecular dynamics simulations to study Kv2.1 channel conduction under the applied membrane voltage with and without RY785 or TEA present. While TEA directly blocks K+ permeation by occluding ion permeation pathway, RY785 binds to multiple nonpolar residues near the hydrophobic gate of the channel driving it to a semi-closed non-conductive state. This mechanism was confirmed using an additional set of simulations and used to explain experimental electrophysiology data.

Strengths:

The total length of simulation time is impressive, totaling many tens of microseconds. The study develops forcefield parameters for the RY785 molecule based on extensive QM-based parameterization. The computed permeation rate of K+ ions through the channel observed under applied voltage conditions is in reasonable agreement with experimental estimates of the singlechannel conductance. The study performed extensive simulations with the apo channel as well as both TEA and RY785. The simulations with TEA reasonably demonstrate that TEA directly blocks K+ permeation by binding in the center of the Kv2.1 channel cavity, preventing K+ ions from reaching the SCav site. The conclusion is that RY785 likely stabilizes a partially closed conformation of the Kv2.1 channel and thereby inhibits the K+ current. This conclusion is plausible given that RY785 makes stable contact with multiple hydrophobic residues in the S6 helix. This further provides a possible mechanism for the experimental observations that RY785 speeds up the deactivation kinetics of Kv2 channels from a previous experimental electrophysiology study.

Weaknesses:

The study, however, did not produce this semi-closed channel conformation and acknowledges that more direct simulation evidence would require extensive enhanced-sampling simulations. The study has not estimated the effect of RY785 binding on the protein-based hydrophobic pore constriction, which may further substantiate their proposed mechanism. And while the study quantified K+ permeation, it does not make any estimates of the ligand binding affinities or rates, which could have been potentially compared to the experiment and used to validate the models. 

As stated in the original manuscript, we concur that the mechanism we propose remains hypothetical until further studies of the complete conformational cycle of the channel are conducted. The recently determined structure of a Kv2.1 channel in the closed state (Mandala and MacKinnon, PNAS 2025) presents an excellent opportunity to do so. Indeed, a cursory analysis of that structure shows that a Pro-Ile-Pro motif in helix S6 marks the position of the intracellular gate, where the pore domain constricts maximally (aside from the selectivity filter). As illustrated in Fig. 5, this motif is precisely where the benzimidazole and thiazole moieties of RY785 bind in our simulations. The mechanism we outline in Fig. 7 thus seems very plausible, in our view; that is RY785 occludes the K⁺ permeation pathway before the pore domain reaches the closed conformation, explaining the observed electrophysiological effects (see Discussion). The Discussion has been revised to note the recent discovery of the aforementioned structure, its implications for the mechanism we propose, and the opportunities for further research that are now open.

Reviewer #3 (Public review):

Summary:

In this manuscript, Zhang et al. investigate the conductivity and inhibition mechanisms of the Kv2.1 channel, focusing on the distinct effects of TEA and RY785 on Kv2 potassium channels. The study employs microsecond-scale molecular dynamics simulations to characterize K+ ion permeation and compound binding inhibition in the central pore. 

Strengths:

The findings reveal a unique inhibition mechanism for RY785, which binds to the channel walls in the open structure while allowing reduced K+ flow. The study also proposes a long-range allosteric coupling between RY785 binding in the central pore and its effects on voltage-sensing domain dynamics. Overall, this well-organized paper presents a high-quality study with robust simulation and analysis methods, offering novel insights into voltage-gated ion channel inhibition that could prove valuable for future drug design efforts.

Weaknesses:

(1) The study neglects to consider the possibility of multiple binding sites for RY785, particularly given its impact on voltage sensors and gating currents. Specifically, there is potential for allosteric binding sites in the voltage-sensing domain (VSD), as some allosteric modulators with thiazole moieties are known to bind VSD domains in multiple voltage-gated sodium channels (Ahuja et al., 2015; Li et al., 2022; McCormack et al., 2013; Mulcahy et al., 2019).

As noted in the manuscript, we designed our simulations to explore the possibility that RY785 binds within the pore domain, because TEA and RY785 are competitive and TEA is known to bind within the pore. That RY785 did in fact spontaneously and reproducibly bind within the pore was however not a predetermined outcome; if the site of interaction for the inhibitor was elsewhere in the channel, the simulation would not have shown a stable associated state, which would have prompted us to examine other possible sites, including the voltage sensors. It was also not predetermined or foreseeable a priori that the mode of interaction we observed in simulation provides a straightforward rationale for the electrophysiological effects of RY785. Based on our results, therefore, we believe that RY785 binds within the pore of Kv2. As stated by the reviewer, other allosteric modulators are known to bind instead to the sensors; to our knowledge, however, there is no precedent of a small-molecule inhibitor that simultaneously acts on the sensors and the pore domain. We therefore believe that future studies should focus on corroborating or refuting the mechanism we propose, through additional experimental and computational work; if, contrary to our claim, RY785 is found not to bind to the pore domain, it would be logical to explore other possible sites of interaction, as the reviewer suggests. The Discussion has been modified to address this point.

(2) The study describes RY785 as a selective inhibitor of Kv2 channels and characterizes its binding residues through MD simulations. However, it is not clear whether the identified RY785-binding residues are indeed unique to Kv2 channels.

To clarify this question, we have included a multiple sequence alignment as Supplementary Figure 1; the revised manuscript refers to this figure in the Discussion section. The alignment reveals that the cluster of residues forming contacts with RY785 (Val409, Pro406, Ile405, Ile401, and Val398) is indeed specific to Kv2.1. Among Kv channels, Kv3.1 and Kv4.1 exhibit the greatest similarity to Kv2.1 at these positions, but they differ in a crucial substitution: Ile405 in Kv2.1 is replaced by Val. This replacement shortens the sidechain, undoubtedly reducing the magnitude of the hydrophobic interaction between inhibitor and channel (Val is approximately 6 kcal/mol, i.e. 1,000 times, more hydrophilic than Ile). Kv5.1 differs from Kv2.1 at two positions: Pro406 is replaced by His, and Val409 by Ile. The introduction of His abolishes the hydrophobic interaction at that position, and the need for hydration likely perturbs all adjacent contacts with RY785. Lastly, Kv6-Kv10 and Cav channels feature entirely different residues at these positions. Consistent with these findings, a recent study by the Sack lab (https://elifesciences.org/articles/99410) has demonstrated that Kv5, Kv6, Kv8, and Kv9 pore subunits confer resistance to RY785, while a high-throughput electrophysiological study carried out by Merck (Herrington et al., 2011) reported that RY785 shows no significant activity against Cav channels. The sequence alignment offers a simple interpretation for these experimental observations, namely that RY785 is recognized by Kv2 channels through the abovementioned hydrophobic cluster within the pore domain.

(3) The study does not clarify the details, rationale, and ramifications of a biasing potential to dihedral angles.

We refer the reviewer to published work, for example Stix et al, 2023 and Tan et al, 2022. We provide additional comments below.

(4) The observation that the Kv2.1 central pore remains partially permeable to K+ ions when RY785 is bound is intriguing, yet it was not revealed whether polar groups of RY785 always interact with K+ ions.

We detected no persistent specific interactions between RY785 and the permeant K+ ions.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The manuscript describes atomistic molecular dynamics (MD) simulations of a voltage-gated potassium channel Kv2.1 using its cryo-EM structure in the open activated state and its inhibition by a classical non-specific cationic blocker tetraethylammonium (TEA) as well as a novel selective inhibitor RY785. Using multi-microsecond-long all-atom MD runs under the applied membrane voltage of 100 mV the authors were able to confirm that the channel structure represents an open conducting state with the computed single-channel conductance lower than experimental values, but still in the same order of magnitude range. They also determined that both TEA and RY785 bind in the channel pore between the cytoplasmic hydrophobic gate and narrow selectivity filter (SF) region near the extracellular side. However, while TEA directly blocks a knock-on K+ conduction by physically obstructing ion access to the SF, the mechanism of action of RY785 is different. It does not directly prevent K+ access to the SF but rather binds to multiple residues in the hydrophobic gate region, which effectively narrows a pore and drives the channel toward a semi-closed nonconductive conformation, which might be distinct from one with the deactivated voltage sensors and closed pore observed at hyperpolarized membrane potentials. However, additional studies beyond the scope of this work might be needed to fully establish this mechanism as suggested by the authors.

The manuscript is written very well and represents a significant advance in the field of ion channel research. I do not have any major issues, which need to be addressed. However, I have several suggestions.

For the apo-channel K+ conduction MD simulation under the applied voltage, the authors seem to observe mostly a direct or Coulomb knock-on mechanism across the SF with almost no water copermeation. This is in line with computational electrophysiology studies with dual membrane setup by B. de Groot and others but in disagreement with multiple previous studies by B. Roux and others also using applied electric field and CHARMM force fields as in the present study. I wonder why the outcomes are so different. Is it related to the Kv2.1 channel itself, a relatively small applied electric field used (corresponding to a membrane potential of 100 mV vs. 500-750 mV used in many previous simulations), ion force field (e.g., LJ parameters), or some other factors? Could weak dihedral restraints on the protein backbone and side chains contribute to this mechanism? I also wonder if the authors might have considered different initial SF ion configurations. Related to that, I wonder if the authors observed any SF distortions in their simulations including frequently observed backbone carbonyl flipping and/or dilation/contraction.

We are aware of these discrepancies between published simulation studies, but cannot offer a satisfactory explanation, beyond speculation. The reviewer is correct that the mechanism of ion permeation we observe is comparable to that reported by de Groot, as we noted in Tan et al, 2022 and Stix et al, 2023. Neither in this nor in those previous studies did we observe any persistent distortions of the selectivity filter – but that outcome was expected by construction. The weak biasing potentials acting on the mainchain dihedral angles allow for local fluctuations but not a persistent deformation, relative to the conductive form determined experimentally.

For MD simulations with the ligand present, I wonder if the authors can comment on the effect of the ligand especially RY785 on the pore size or more importantly size of the hydrophobic gate. The presence of the ligand itself would definitely result in a narrower pore, but I also wonder if this would also lead to a rearrangement of pore sidechain and/or backbone residues, which would lead to a narrower pore from a protein itself thus confirming the proposed mechanism of driving the channel towards a semi-closed state. It is easy to compute but I wonder if the presence of weak dihedral restraints may preclude this analysis.

Yes, while the simulation design used in this study allows for local fluctuations in the mainchain structure and nearly unrestricted sidechain dynamics, changes in either the secondary or tertiary structure of the channel are strongly disfavored. This approach is thus sufficient to examine ligand binding or ion flow in the microsecond timescale but not channel gating. In the revised version of the Discussion, we outline a roadmap for future computational studies of that gating process, on the basis of the open-channel structure we used and the recently determined structure of the closed state.

The authors state that RY785 does not block K+ ion, but it does significantly slow the rate of K+ ion access to the pore Scav site. Is this not a part of the mechanism for inhibition of the channel? The authors seem to focus on the primary mechanism of inhibition as the RY785 promoting channel closing, but would it not also reduce K+ current in the open state by slowing the rate of K+ entry into the cavity and selectivity filter? The authors should address this point in the text. I am also somewhat confused that in the MD simulations performed by the authors, there is still some K+ conduction with RY785 in the pore, which is not in 100% agreement with electrophysiology experiments. Does it mean that the channel in the simulations has not yet reached that semiclosed state or a reduced K+ conduction is not observed experimentally?

The salient experimental observation is RY785 abrogates K+ currents through Kv2 channels (Herrington et al, 2011; Marquis et al, 2022). In our view, that observation can be explained in one of two ways: either RY785 completely blocks the flow of K+ ions across the channel while the pore domain remains in the conductive, open state – like TEA does – or RY785 induces or facilitates the closing of the channel, thereby abrogating K+ flow. The fact that we observe K+ flow while RY785 is bound to the channel is therefore not in disagreement with the electrophysiological measurements, but it does rule out the first of those two possible interpretations of the existing experiments. As it happens, the second possible explanation, i.e. that RY785 facilitates the closing of the pore domain, also provides a rationale for another puzzling experimental observation, namely that RY785 shifts the voltage dependence of the currents produced by the voltage sensors as they reconfigure to open or close the intracellular gate.

Also, I wonder if the authors considered that since there are 4 potential equivalent sites in the pore (although, overlapping) more than one RY785 might be needed to prevent K+ conduction, even though the experimental Hill coefficient of ~1 does not indicate cooperativity.

Admittedly, our simulation design was based on the premise that only one RY785 molecule might be recognized within the pore. Based on the outcome of the simulations, we are confident that this assumption was valid, as the binding pose that we identified rules out multiple occupancy – which would be indeed consistent with a Hill coefficient of ~1.

I also wonder if the authors considered estimating ligand binding affinities and/or "on" rates from their simulations to have a more direct comparison with experiments and test the accuracy of their models. There are multiple enhanced sampling techniques allowing to do that, although it can be a study on its own.

We thank the reviewer for this suggestion, which we will consider for future studies.

The authors also discussed that they could not study Kv2.1 deactivation in a reasonable simulation time. Indeed it is very challenging but they should cite previous studies e.g. 2012 Jensen et al paper (PMID: 22499946) on this subject. There are structures of Kv channels with the deactivated voltagesensing domains (VSDs) available, e..g of EAG1 channel (PDB 8EP1), although they do not have a domain-swapped architecture. There are structural modeling approaches including AlphaFold, which can be potentially used to get a Kv2.1 structure with deactivated VSDs, and targeted MD, string method etc. can be used to study transition between different states with and without bound ligands.

As noted, a structure of a Kv2 channel with a closed pore has now been determined experimentally. In the revised Discussion, we comment on what this structure tells us about the mechanism of inhibition we propose, and how it could be leveraged in future studies.

The authors should be commended for doing a thorough QM-based force field parameterization of RY785. However, a validation of the developed force field parameters is lacking. In terms of QM validation, a gas-phase dipole moment can be compared in terms of direction and magnitude (it's normal to be overestimated to implicitly reflect solvent-induced polarization). If there are any experimental data available for this compound, they can be tested as well.

We agree with the reviewer that forcefield validation is important, but to our knowledge no experimental data exists for RY785 to compare with, such as hydration free energies. We did however compare the gas-phase dipole moment computed with QM and with the MM forcefield we developed based on atomic charges optimized to reproduce QM interactions with water. The MM model yields a gas-phase dipole moment of 3.94 D, which is 20% greater than the QM dipole moment, or 3.23 D. That deviation is within the typical range for electroneutral molecules (Vanommeslaeghe et al, 2010), and as the reviewer notes, reflects the solvent-induced polarization implicit in the derivation of atomic charges. As shown in Author response image 1, the orientation of the dipole moment calculated with MM (right, blue arrow) is also in good agreement with that predicted with QM (left)

Author response image 1.

(1) p. 3 "the last two helices in each subunit" -> "the last two transmembrane helices in each subunit".

Thanks. Corrected.

(2) p. 5 "and therefore do not cause large density variations e.g. 100-fold or greater.". I would be more specific here and indicate what are the actual variations in density or free energy encountered and how they are compared e.g. with thermal fluctuations (~kT).

Thanks. The exact variations in K+ density had been included in the original manuscript, in Fig. 2C, but we failed to refer to this figure at this point in the description of the results. The ion density is plotted in a log scale to facilitate conversion to free-energy units. Corrected.

(3) p. 6 Figure 1 caption "and along the perpendicular to the membrane" -> "perpendicular to the membrane normal"?. "The channel is an assembly of four distinct subunits (in colors);" -> "The channel is an assembly of four identical subunits (distinct by colors);". I would use the same protein coloring method in panels B and C as was used in panel A.

Thanks. Corrected as needed.

(4) p. 6 Figure 2 In panel B I would appreciate a representative complete ion permeation event trace. In panel C caption I would indicate corresponding sites "S0-S4, Scav" for each residue mentioned. I also would not use gray color for site names in the figure.

We appreciate the suggestion, but believe the figure is clear as is. Panel B is meant to focused on the mechanism of knock-on. Panel A includes numerous complete permeation events. 

(5) p. 7 Figure 3 caption. Please indicate which atoms of residues T373 and P406 were used to define SF and gate positions. Chemical structures of both TEA and RY785 would be useful. In panels C and F channel interacting residues (if any) would be helpful to show.

The revised caption clarifies that the positions of T373 and P406 are represented by their carbonalpha atoms. A close-up view of the structures of TEA and RY785 is included in the Supplementary Information section.

(6) p. 8. Figure 4 caption. Please indicate if N atoms ere used for density maps in panels B and C, and which value of the density was used to show meshes. In panel A please indicate what are the units of the density shown by color maps. 

The caption has been revised to clarify these questions.

(7) p. 9 "inside the protein" -> "inside the channel pore".

Thanks. Corrected.

(8) p. 10 "which lines the cavity" -> "which lines the water-filled cavity"

We appreciate the suggestion but believe the wording is clear as is.

(9) p.10 Fig. 5. It would be helpful to distinguish residues from different chains e.g. by different colors rather than using different colors for different residues. The S atom in RY785 is hard to recognize due to the yellow color used for C atoms. Figure 5B is very confusing. It is not clear what this plot represents. For instance, what does it mean that Pro405 has ~10 contacts in 20% of simulation snapshots? Does it mean 10 C..C/S interactions within 4.5 A? I am not sure what the value of this is. I think a bar or radar chart plot showing % of contacts with one, two, or more residues of each type would be more helpful. 

Thanks. The revised caption ought to clarify how to interpret the plot.

(10) p. 12 "Due to its 2-fold molecular symmetry". TEA has a tetrahedral point group or Td symmetry. It has several two-fold rotational axes though. 

Thanks. Corrected.

(11) p. 12 "it prevents K+ ions in the cytoplasmic space from destabilizing the K+ ions that reside in the selectivity filter" I am not sure if this statement is entirely accurate as there might be destabilization of a multi-ion SF configuration not ions per see.

We believe this statement is clear as is.

(12) p. 13 Fig. 7 caption "includes non-conductive or transiently inactivated states" - I am not sure what "transiently inactivated state" is as inactivation is a specific term used in ion channel research and it does not seem to be explicitly considered in this study.

A reference has been included in the caption for readers interested in the process of inactivation.

(13) p. 14 "the net charge of these constructs is thus zero". This would depend on the number of basic and acidic residues in the protein. 

Yes, it does – and as a result the construct we model has a net zero charge.

(14) p. 14 I wonder if the protein was constrained or heavily restrained during MARTINI membrane building and equilibration procedure. Otherwise, C-alpha mapping would be problematic and clashes with lipid membrane atoms might take place as well.

It was indeed. When a protein is simulated using the MARTINI coarse-grained forcefield, its fold must be preserved through a network of strong ‘virtual’ bonds between adjacent carbon-alpha atoms. This is standard practice so we do not believe it requires further explanation.

(15) p. 15 PME - please spell out and provide reference.

Corrected.

(16) p. 15 "with a smooth switching function" - is it a special or standard switching function? Also, was it used for energy or forces? 

The switching function brings both forces and energies to a value of zero at the cut-off value, smoothly. We refer the reviewer to the NAMD manual for further details.

(17) p. 15 '𝑘 = 1 𝑘B𝑇.' Please confirm that there is a factor of "1" there, which can be actually skipped if this is the case. 

The value of k = 1 KBT is correct.

(18) p. 15. Please cite PMID: 22001851 for the transmembrane electric field application technique.

Corrected.

(19) p. 15 "and CHARMM36m" -> "and CHARMM36m force field". 

Corrected.

(20) p. 16 "the four proteins subunits" -> "the four protein subunits". 

Corrected.

(21) p. 16. Please provide the reference for CGenFF. It's reference 49. 

Corrected.

Supporting Information (SI): CGenFF is misspelled in multiple figure captions in the SI. All potential energy scans indicate "angle", but some are bond angles while others are dihedral angles. Using subscripts for atom numbers is confusing and does not match the numbering scheme used in Fig. S1. So, please use the same style of numbering throughout, e.g. C46-C42-N43 (without subscripts). Please label the X and Y axes in Figsures S2-S19 and S21. In Figure S22 please perform a linear regression analysis and/or compute Pearson correlation coefficients and indicate trend lines. Table S1. It would be good to compute RMS or mean unsigned errors to get an idea about accuracy. Also, please indicate if reference QM values were scaled by 1.16 for energies or offset for distances. 

The Supplementary Information has been corrected. We thank the reviewer for their detailed feedback. 

Reviewer #3 (Recommendations for the authors):

(1) The study needs to consider the possibility of multiple binding sites for RY785, particularly given its impact on voltage sensors and gating currents. Specifically, the potential for allosteric binding sites in the voltage-sensing domain (VSD) should be assessed, as some allosteric modulators with thiazole moieties are known to bind VSD domains in multiple voltage-gated sodium channels (Ahuja et al., 2015; Li et al., 2022; McCormack et al., 2013; Mulcahy et al., 2019). Molecular docking and/or MD simulations could quickly test this hypothesis. If this hypothesis is not true, a comprehensive search can exclude such a possibility, which can also confirm the long-range allosteric coupling between RY785 binding in the central pore and voltage-sensing domain dynamics. 

Please see our response above.

(2) The authors describe RY785 as a selective inhibitor of Kv2 channels and characterize its binding residues through MD simulations. To support this claim, Figure 5 needs to include a multiple sequence alignment with other Kv channels. This would help demonstrate whether the identified RY785-binding residues are indeed unique to Kv2 channels.

Please see our response above.

(3) The study applies a biasing potential to 𝜙, 𝜓, and 𝜒1 dihedral angles. Please clarify:

(a) Is this potential solely to prevent selectivity filter collapse/degradation, as mentioned in a previous D. E. Shaw Research publication (Jensen et al., 2012)?

Yes, that is correct.

(b) If it applies to all amino acids, can this potential prevent other changes, such as in the voltagesensing domain?

Yes, that is correct.

(c) What specific "large-scale structural changes" does this potential preclude? 

For example, it would preclude the spontaneous degradation of the secondary or tertiary structure of the protein. We have revised the Methods section to make these points clearer. 

(d) Given that such biasing potentials on backbone dihedral angles can decrease conformational flexibility, and considering that Kv channel permeability/conductivity could be highly sensitive to filter flexibility, what insights can you provide about the impact of the force constant k on channel conductivity?

In previous studies based on an identical methodology (Stix et al, 2023; Tan et al, 2022), we have observed good agreement between calculated and experimental conductance values – at least as good as can be hoped for, when all approximations are considered. Based on the data presented in those studies, we have no reason to believe our methodology inhibits the permeability of the channel, which is logical as the local structural fluctuations required for K+ flow across the selectivity filter are not impaired, by definition. To the contrary, the fact that these weak biasing potentials make the conductive form of the filter the most favorable state in simulation enable a clear-cut analysis of conductance under plausible simulation conditions, both in terms applied voltage and K+ concentration. We refer the reviewer to the abovementioned studies for further details and a discussion of this subject.

(4) The observation that the Kv2.1 central pore remains partially permeable to K+ ions when RY785 is bound is intriguing. Given the compact nature of the central cavity when RY785 is bound, it would be valuable to investigate whether polar groups of RY785 (e.g., nitrogens from the amide, benzimidazole, and thiazole moieties) always interact with K+ ions. Characterizing these interactions could inform the design of similar compounds with differential modulation effects.

We examined this possibility and detected no convincing interaction patterns between RY785 and K+ ions – logically, inhibitor and ions are in close proximity while residing concurrently within the pore, but we detected no evidence of specific interactions.

Minor points:

It is strongly recommended that the refined force field parameters for RY785 be shared as a separate supplementary file in CHARMM force field format. This addition would be valuable for the scientific community, allowing other researchers to use or compare these parameters in future studies.

We agree entirely. Upon publication of the VOR for this article the forcefield parameters for RY785 will be made freely available for download at https://github.com/Faraldo-Gomez-Lab-atNIH/Download.

The study uses a KCl concentration of 300 mM, which exceeds typical intracellular K+ levels. While this may be intentional to enhance K+ permeation probability, a brief justification for this choice should be included in the Methods section.

Yes, what motivated this choice in this and in our previous studies of K+ channels was the expectation of a greater number of permeation events, for a given simulation length, and therefore greater confidence (i.e. statistical significance) in the observed ion conductance, or in the degree to which it might be inhibited by a blocker. It worth noting that 300 mM KCl, while atypical in the intracellular environment, is often used in electrophysiological studies. The Methods section has been amended to clarify this point.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Persistence is a phenomenon by which genetically susceptible cells are able to survive exposure to high concentrations of antibiotics. This is especially a major problem when treating infections caused by slow growing mycobacteria such as M. tuberculosis and M. abscessus. Studies on the mechanisms adopted by the persisting bacteria to survive and evade antibiotic killing can potentially lead to faster and more effective treatment strategies.

To address this, in this study, the authors have used a transposon mutagenesis based sequencing approach to identify the genetic determinants of antibiotic persistence in M. abscessus. To enrich for persisters they employed conditions, that have been reported previously to increase persister frequency - nutrient starvation, to facilitate genetic screening for this phenotype. M.abs transposon library was grown in nutrient rich or nutrient depleted conditions and exposed to TIG/LZD for 6 days, following which Tnseq was carried out to identify genes involved in spontaneous (nutrient rich) or starvationinduced conditions. About 60% of the persistence hits were required in both the conditions. Pathway analysis revealed enrichment for genes involved in detoxification of nitrosative, oxidative, DNA damage and proteostasis stress. The authors then decided to validate the findings by constructing deletions of 5 different targets (pafA, katG, recR, blaR, Mab_1456c) and tested the persistence phenotype of these strains. Rather surprisingly only 2 of the 5 hits (katG and pafA) exhibited a significant persistence defect when compared to wild type upon exposure to TIG/LZD and this was complemented using an integrative construct. The authors then investigated the specificity of delta-katG susceptibility against different antibiotic classes and demonstrated increased killing by rifabutin. The katG phenotype was shown to be mediated through the production of oxidative stress which was reverted when the bacterial cells were cultured under hypoxic conditions. Interestingly, when testing the role of katG in other clinical strains of Mab, the phenotype was observed only in one of the clinical strains demonstrating that there might be alternative anti-oxidative stress defense mechanisms operating in some clinical strains.

Strengths:

While the role of ROS in antibiotic mediated killing of mycobacterial cells have been studied to some extent, this paper presents some new findings with regards to genetic analysis of M. abscessus susceptibility, especially against clinically used antibiotics, which makes it useful. Also, the attempts to validate their observations in clinical isolates is appreciated.

Weaknesses:

Amongst the 5 shortlisted candidates from the screen, only 2 showed marginal phenotypes which limits the impact of the screening approach.

We appreciate the reviewer’s comments, but we note that 4 out of 5 genes displayed phenotypes concordant with findings of the Tn-Seq data, with katG and pafA, as well as MAB_1456c (during starvation only) and blaR (in rich media only) having decreased survival as shown in Figure 3A-D. We do agree that some of the phenotypes were more modest in a single-mutant context than in the pooled Tn-Seq screen. In addition, several mutants that had modest changes in survival also showed profound defects in resuming growth after removal of antibiotics, with the pafA mutants particularly impaired. (Figure 3 - figure supplement 1).

While the role of KatG mediated detoxification of ROS and involvement of ROS in antibiotic killing was well demonstrated, the lack of replication of this phenotype in some of the clinical isolates limits the significance of these findings.

While the role of katG varied among strains, the antibiotic-induced accumulation of ROS was seen in all three strains (Figure 6A). This suggests that in some strains other ROS-detoxification pathways are able to compensate for the loss of katG.

(Figure 2—figure supplements 1–3)

Figure 1—figure supplement 1.

Reviewer #2 (Public review):

Summary:

The work set out to better understand the phenomenon of antibiotic persistence in mycobacteria. Three new observations are made using the pathogenic Mycobacterium abscessus as an experimental system: phenotypic tolerance involves suppression of ROS, protein synthesis inhibitors can be lethal for this bacterium, and levofloxacin lethality is unaffected by deletion of catalase, suggesting that this quinolone does not kill via ROS.

Strengths:

The ROS experiments are supported in three ways: measurement of ROS by a fluorescent probe, deletion of catalase increases lethality of selected antibiotics, and a hypoxia model suppresses antibiotic lethality. A variety of antibiotics are examined, and transposon mutagenesis identifies several genes involved in phenotypic tolerance, including one that encodes catalase. The methods are adequate for making these statements.

Weaknesses:

The work can be improved by a more comprehensive treatment of prior work, especially comparison of E. coli work with mycobacterial studies.

Moreover, the work still has some technical issues to fix regarding description of the methods, supplementary material, and reference formating.

See detailed responses below.

Overall impact: Showing that ROS accumulation is suppressed during phenotypic tolerance, while expected, adds to the examples of the protective effects of low ROS levels. Moreover, the work, along with a few others, extends the idea of antibiotic involvement with ROS to mycobacteria. These are fieldsolidifying observations.

Comments on revisions:

The authors have moved this paper along nicely. I have a few general thoughts.

It would be helpful to have more references to specific figures and panels listed in the text to make reading easier.

Text modified to add more figure references.

(1) I would suggest adding a statement about the importance of the work. From my perspective, the work shows the general nature of many statements derived from work with E. coli. This is important. The abstract says this overall, but a final sentence in the abstract would make it clear to all readers.

We appreciate the suggestion and have added a line to the abstract.

(2) The paper describes properties that may be peculiar to mycobacteria. If the authors agree, I would suggest some stress on the differences from E. coli. Also, I would place more stress on novel findings. This might be done in a section called Concluding Remarks. The paper by Shee 2022 AAC could be helpful in phrasing general properties.

We have added mention of this in the discussion (lines 354-356).

(3) Several aspects still need work to be of publication quality. Examples are the materials table and the presentation of supplementary material. Reference formatting also needs attention.

We respond to the specific details below.

Reviewer #3 (Public review):

Summary:

The manuscript demonstrates that starvation induces persister formation in M. abscesses.

They also utilized Tn-Seq for the identification of genes involved in persistence. They identified the role of catalase-peroxidase KatG in preventing death from translation inhibitors Tigecycline and Linezolid. They further demonstrated that a combination of these translation inhibitors leads to the generation of ROS in PBS-starved cells.

Strengths:

The authors used high-throughput genomics-based methods for identification of genes playing a role in persistence.

Weaknesses:

The findings could not be validated in clinical strains.

Comments on revisions: No more comments for the authors.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors are strongly encouraged to check the references. There is some systematic error in the citations of references. Started to list but then they were too many.

For example Ln 51, Ref #11 cited, should be #10. Ln 59, #18 is wrongly cited. Should be - Ln 104. Ref #27 wrongly cited.

Ref #26 and #28 identical.

Even in discussion section a lot of references are mis-cited.

We very much appreciate the reviewer catching this issue with the import of our references and we have corrected this.

Reviewer #2 (Recommendations for the authors):

Below I have listed comments on specific issues that I hope are useful during revision.

Line 21 population is singular

Text modified

Line 21 comma after antibiotic (subordinate clause) Line

Text modified

25 is how singular?

Text modified

Impression of abstract: the work seems to confirm and therefore generalize concepts derived from studies with E. coli. If the authors agree, such a statement would be appropriate as a final sentence. I would also look for novel features to stress in the abstract.

Line 41 this challenge is vague

Text modified

Line 43 comma such as (also comma at the end of the parenthetical statement). This type of comma error is common throughout the manuscript and slows reading.

Text modified

Line 60 paradoxically. Is this the best concept? Or is it the natural effect of evolution (assuming that mycobacteria or their ancestors were exposed to environmental antibiotics)?

It is certainly problematic for clearing infection.

Text not modified.

Line 63 highlighted uncertainties ... meaning is unclear especially since you may have changed what "model" is referring to.

Text modified

Line 66 models.... Do you really mean systems? Models of what?

This refers to mechanistic models. Text not modified.

Line 67 arrest cell division. This is written as if it were true. Does the evidence point specifically to cell division or perhaps more accurately suppression of metabolism (see Ye et al 2025 mBio).

Both have been postulated as important. Text modified to add concept of metabolism

... targeted by antibiotics non-essential... Do you think that antibiotics work by inactivating essential targets? That seems overly simplistic, as lethal action is more likely the metabolic response to the damage caused. By the end of the paragraph you come around to this view, but you have already misdirected the reader. The reader is not sure what to believe. Line 70 note that there are many inhibitors of transcription and translation that only block growth, they do not rapidly kill cells

There can be both direct, and indirect secondary killing mechanisms. We devote a significant portion of the Discussion section to this topic.

Line 71 debate. There was indeed a debate, but reference 22 is not a valid citation for this. I think you mislead the reader by not accurately describing the debate. It was basically about the inability of Kim Lewis and James Imlay to reproduce the work of ref. 22. A great deal of prior work and then subsequent work showed that the challenge to ref. 22 lacked substance.

(1) Text modified to fix an error in the citation number related to direct β-lactam-mediated lysis.

(2) We agree that there is a great deal of data supporting antibiotic-induced ROS as important for bactericidal activity in many circumstances and do not argue otherwise. This sentence points out that over the years the paradigm for how antibiotics kill bacteria has evolved.

Line 80. It seems you are starting a new topic here. What about beginning a new paragraph?

The paragraph introduces mycobacteria of which Mabs is one. Text not modified.

Line 85 delete the comma: it implies a compound sentence that is not delivered.

Text modified.

Line 109 screen singular

Text modified.

Line 156 these conditions is imprecise and vague

Conditions were described in paragraph above in the manuscript. Text not modified.

Fig 2 it would be helpful to more clearly define the meaning of the coordinates

Text modified.

Line 230 and throughout please indicate the location of the data being cited for rapid reader reference

Text modified.

Lines 315-323 You could use this paragraph as the first of the Discussion. Some readers prefer to read the Discussion before the results. For them, a summary at the beginning of the Discussion is useful.

Text modified.

Line 328 without underlying mechanism... for E. coli refer to Zeng PNAS 2022. Depending on when the final version of this paper happens, there should be a figure in a Zhao Zhu mLife paper on purA that will have been published. Since it is not yet available, it cannot be cited.

We agree that the Zeng et al study is interesting and have added this reference to our discussion. However, these findings related to broad Crp-regulated tolerance actually underscore the point that we are making: that there are multiple factors (Crp, RelA, Lon, TisB, MazE, others) that mediate antibiotic tolerance.

Line 339 where are the data?

These data are in Figure 5, panels C, D. We have clarified the text to indicate that only a single agent from each of these classes was tested.

Line 346 here you are summarizing evidence for ROS in killing mycobacteria. You should include the moxifloxacin study by Shee et al 2022 AAC.

Reference added.

Line 348 refer to James Collins' work with E. coli in which his lab examined agents with a variety of mechanisms. There seems to be a fundamental difference between E. coli and mycobacteria with respect to rifampicin, a strictly static agent in E. coli but clearly lethal in mycobacteria. Note that chloramphenicol is static in E. coli and blocks ROS production. What does it do in mycobacteria? A brief discussion of this difference might be relevant at line 362

Text modified.

Lines 364-368 Here the idea might be simply that there are two modes of killing, one that is a direct extension of class-specific damage (chromosome fragmentation with fluoroquinolones, for example, or cell lysis by beta-lactams) and a second that is a metabolic response to the antibiotic damage (ROS accumulation). The second type is not class specific. Within this context, the mycobacterial killing by rifampicin might be a class-specific extension of inhibition of transcription that does not occur in E. coli.

Agreed, text modified to include this.

Line 400 The Key Resource table is not of publication quality. Precision and repeatability can be improved by spelling out the name of the vendor and its location (City, Country). In the present case, use of BD is lab jargon.

We appreciate the reviewer’s precision. However, this is actually not lab jargon. Becton, Dickinson and Company now refers to itself as BD (see https://www.bd.com/en-us), and the American Type Culture Collection now refers to itself as ATCC (see https://www.atcc.org/about-us/who-we-are).

Line 639 It would be good to have experienced colleagues critically review the manuscript, especially for English usage. Listing those persons here adds to the credibility of the work

Text not changed.

References: please refer to the journal style. Here you use italic for titles and scientific names, thereby obscuring the scientific names. Normally article titles are not italic and scientific names are ALWAYS italic unless prohibited by journal style.

Our reference format is concordant with eLife submission guidelines, and all references are reformatted by the journal at the time of final publication (see https://elifesciences.org/insideelife/a43f95ca/elife-references-yes-we-take-any-format-no-we-re-not-rekeying).

Supplemental Material: Please refer to journal style. Normally this is a stand-alone document that includes a title page and carefully crafted figure legends. Supplemental figures would be numbered as 1, 2, ... A professional appearing Supplemental Material section shows author publication experience not obvious in other parts of the paper. The text indicated MIC determinations. I would like to see a table of MIC values.

(1) MIC table added as Supplemental Table 5.

(2) The Supplemental figures are submitted and named in accordance with eLife instructions. Please note that for eLife, there is not a stand-alone supplementary figure section with a title page as you are requesting, but instead the figure supplements for each figure are provided as online files linked to each figure.

Reviewer #2 (Public review):

Summary

The aim of this study was to assess which amino acid stretches are tolerated/favoured in the course of evolution, considering their physico-chemical properties, metabolic costs and proteotoxicity. To address this question, the authors expressed PolyX variants in yeast, E. coli and also referred to COS cells. The PolyX constructs were tagged with GFP or a different fluorescence reporter to assess expression levels and localization at the C-terminus with or without a cleavable linker or to study topological effects. The PolyX stretch was also embedded between two different fluorescent proteins. The authors used growth rate and expression levels as judged by fluorescence intensities to calculate the relative neutrality in comparison to GFP alone.

They could show that harmful/beneficial effects depend on the specific amino acid (aa) and polar aa are tolerated well, whereas hydrophobic and positively charged aa are harmful to the cell. This is not surprising as hydrophobic and positively charged aa are known to be aggregation-prone. They could further show that the topology matters for some, but not all, PolyX variants. The PolyX stretch can affect the subcellular localization and aggregation propensity of the GFP it is fused to. Interestingly, overexpression of PolyG, PolyQ or PolyS was not harmful, and overexpression of PolyE was potentially even beneficial for the cell. The authors concluded their study with a theoretical analysis of the presence of aa stretches in various species and identified a high correlation between their expression in yeast and other species, suggesting that the selection of aa stretches is conserved and follows biochemical rules (trade-off between tolerance of expression levels, solubility, sub-cellular localization, and maybe metabolic costs).

Strengths:

The authors performed a high number of experiments and systematically assessed the expression and tolerance of 10mer stretches of 20 aa fused to GFP or other fluorophores in yeast and E. coli. This is an impressive effort.

Weaknesses:

(1) The analysis of expression levels of the various PolyX variants should not rely only on fluorescence intensities. The fusion of the PolyX stretch may affect the fluorescence properties (brightness, photostability) of the fluorescent partner and may or may not affect abundance. A quantitative analysis of PolyX-GFP (same applies to the other fusion constructs shown in Figure 3) is needed. Preferably by an MS-based proteomic analysis via peptide count. Western blot is less ideal as it would rely on epitope recognition of the respective antibody, and the epitope accessibility might be altered upon fusion with different PolyX stretches. In addition, the authors should analyse the PolyX stretch without an attached fluorophore as a control.

(2) The images shown in Figure 4 are not very informative. The constructs should be subjected to FRAP to assess the solubility of the PolyX variants and Ssa1 (Hsp70). FCS could be an alternative as well.

(3) The observation of the lack of mCherry fluorescence for PolyK and PolyP (Figure 4) can also be interpreted as an instability of the fusion protein (partial truncation and degradation) or quenching. The authors should test different fluorophores and different linker lengths between the PolyX stretch and the fluorophores. Fluorophore swapping (N/C-terminally) would also be a good control.

(4) The study would benefit from a consideration of a large body of literature on protein aggregation and the contribution of amino acid composition. The here identified amino acids that as 10mer stretch are harmful to the cell and are known to be aggregation-prone and are also recognised by molecular chaperones to prevent their aggregation.

(5) The study could further benefit from ex vivo and in vitro analyses of the PolyX constructs. They could isolate the PolyX variants and study their solubility by, e.g. light scattering outside of the cellular context.

Reviewer #1 (Public review):

Summary:

This manuscript describes a putative clinical association between ARID5B genetic variants and a novel neurodevelopmental syndrome characterized by global developmental delay, intellectual disability, and occasional neuroinflammatory episodes. While the identification of 29 individuals with overlapping phenotypes and the use of a CRISPR-Cas9 mouse model suggest a potential gene-disease link, the study suffers from significant methodological gaps in variant prioritization and a lack of robust mechanistic evidence to support its primary claims. Specifically, the "neuroinflammation" component is over-emphasized despite appearing in only a minor subset of the cohort, and the molecular pathogenesis remains insufficiently explored beyond initial protein localization assays.

Strengths:

(1) The study proposes a new clinical syndrome associated with the ARID5B gene, distinguishing it from established Coffin-Siris syndromes related to other ARID family members.

(2) The recruitment of a relatively large cohort of 29 individuals from diverse geographical and ethnic backgrounds strengthens the initial phenotypic description.

(3) The combination of human clinical data, in vitro localization assays, and an in vivo mouse model provides a multi-level framework for investigating the gene's function.

(4) The identification of variants in the exceptionally long final exon of ARID5B that escape nonsense-mediated mRNA decay (NMD) offers an interesting perspective on the molecular pathology of this gene.

Weaknesses:

(1) The description of the genomic methodology appears limited. A more detailed explanation of the filtration and selection process for variant prioritization is essential. The authors should provide a comprehensive summary of evidence (e.g., CADD scores, allele frequencies in gnomAD, and segregation analysis) to justify the selection of the reported variants, even if they do not strictly meet all ACMG/AMP criteria.

(2) The cohort includes several inherited variants and missense mutations that require more robust evidence of pathogenicity. For example, the presence of the variant in population databases (gnomAD) suggests the need for careful re-evaluation of its causality. A more rigorous assessment using diverse computational metrics, such as PhyloP scores and conservation analysis, is necessary to confirm the pathogenicity of the missense variants.

It is recommended that the authors re-evaluate the cohort to ensure that only variants with strong evidence of causality are included to maintain a clear genotype-phenotype correlation.

(3) The proposed molecular mechanism would benefit from further empirical support. The claim of NMD escape is currently supported by only a small number of cases, and a much more detailed explanation is also required for the experimental data provided.

Although the mouse model exhibits developmental abnormalities, it does not recapitulate the other systemic features reported in humans. In addition, given that "brain development" is a central theme, the manuscript lacks detailed neuroanatomical data, histopathology, or other molecular biological (e.g., RNA-seq) evidence from brain specimens to substantiate these claims at a molecular level.

(4) The emphasis on "neuroinflammation" in the title may be disproportionate to its observed frequency. Central nervous system inflammation was identified in only a small subset of the cohort (2 of 29 individuals).

Without additional experimental validation, such as immunological challenges in the Arid5b mouse model, it is premature to characterize this as a hallmark feature. Additionally, the inconsistent response to immunotherapy suggests that the autoimmune component requires further investigation.

(5) Supplementary tables require reorganization to improve clarity. The current structures make it difficult for readers to effectively analyze the data, and a more standardized format is recommended.

(6) As the manuscript proposes a novel disease entity, a more comprehensive clinical discussion is warranted. The authors should provide a more systematic description of the core clinical features and, crucially, address the genotype-phenotype correlation. Specifically, a more detailed analysis is required to determine whether the clinical severity or the presence of specific features varies according to the location of the variant or the type of mutation. Such insights are essential for clinicians to differentiate this syndrome from other ARID-related disorders.

Reviewer #3 (Public review):

Summary:

In the present study, through international gene-matching efforts, the authors present 29 individuals with rare, heterozygous ARID5B variants and find that these individuals have a newly recognizable neurodevelopmental syndrome. A recurring clinical syndrome of developmental delay/intellectual disability, behavioral difficulties, renal malformation, and recurrent infections is described. 19 of these variants were confirmed to be de novo, and only one was inherited from an unaffected parent. 24/29 of these variants introduce premature termination codons in the final exon and are predicted to escape nonsense-mediated decay. The ARID5B p.Q522Ter variant was studied in a mouse heterozygous knock-in model, found to be associated with behavioral abnormalities. The well-described genetic and phenotypic data for this cohort provide convincing clinical evidence for a novel neurodevelopmental syndrome. The functional evidence provided is preliminary, and further studies are needed to understand disease mechanisms.

Strengths:

(1) The authors give a good description of a novel clinical syndrome manifesting as developmental delay/intellectual disability, facial dysmorphism, and behavioral challenges.

(2) The authors create a mouse model harboring an Arid5b(Q522*/+) variant and identify subtle behavioral changes.

(3) Attempts are made to functionally characterize a subset of ARID5B variants in human cell lines.

Weaknesses:

(1) The title - "ARID5B mutations cause a neurodevelopmental syndrome with neuroinflammation episodes" - should be revised. 2/29 individuals (7%) had CNS inflammation; this does not appear to be a core feature of the disease and should not be highlighted as such. If this is going to be a feature that is highlighted, then more details are needed. MRI images of cerebellitis and/or ADEM would be helpful, as well as lumbar puncture results and supplemental information detailing the treatment course.

(2) The abstract states that "Remarkably, 19 of 29 variants (66%) cluster within the first quarter of exon 10, are de novo, and escape nonsense-mediated mRNA decay (NMD), which we confirmed for two variants affecting seven individuals." The authors state in the Results that they "indeed found no signs of NMD". In Figure 3f, when assessing for transcript amount, there appears to be a great deal of variability. Three ARID5B variant lines are tested. Transcript amounts in two lines appear to be near control levels, but one LCL ARID5B Ile497AsnfsTer31 line appears to demonstrate significantly lower levels of transcript. The control lines also show a great deal of variability. No explanation is given for this large difference between LCL ARID5B Ile497AsnfsTer31 lines and for the variability in control lines, making these data uninterpretable. A major theme of the paper is that early truncating variants in exon 10 escape NMD and lead to the described phenotypes, so this is an important point that needs to be resolved, either by testing more patient-derived lines or knocking in these variants into cell lines.

(3) The Arid5b(Q522*/+) mice are not sufficiently molecularly characterized. Does the variant transcript escape NMD? What happens at the protein level? Is there mislocalization of the protein?

(4) For the HEK293T cell experiments, variants are overexpressed and compared to a control. These experiments appear to leave endogenous ARID5B intact. What might the authors expect to see if these variants were knocked in?

(5) The functional consequences of the missense variants are not tested. The authors suggest that missense variants may be more associated with macrocephaly and possibly ASD. Are these missense variants causing loss-of-function or gain-of-function? Is there preserved protein function?

(6) There are a number of functional assays performed, but it remains unclear if the tested variants are operating through a loss- or gain-of-function. Are truncating variants early in exon 10 leading to a partial loss-of-function? Or do they prevent the functioning of the other allele through a dominant negative mechanism? These possibilities are not directly tested.

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Referee #3

Evidence, reproducibility and clarity

Perez-Rico et al use dCAS9 to activate and repress L1 expression levels in the subfamily level for younger mouse L1s to address their cisregulatory potential

They choose to transcriptionally perturb full-length L1s subfamily.

An important topic, and I liked the approach of using CRISPR to perturb an entire subfamily of transposable elements. However, this study has yet to add any new findings or conclusions. This study can be improved by further analysis or experimentation. The regulatory role of L1s in cis-regulatory function has been previously demonstrated in mouse and human stem cell systems using multiple approaches, including CRISPR-mediated perturbations, CRISPR-based deletions, and 3D chromatin structure analysis. My main concern is the analysis is very superficial and lacks integration of other datatypes such as HiC to further support the role of L1s in enhancer activity and further validation on candidate loci. One of the major limitations of CRISPR-based perturbations is that it can be difficult to conclude the cis-regulatory role of these targeted elements (L1) as synthetic tethering of VPR or KRAB domain can indirectly spread their effect in cis, which otherwise may not have a specific cis-regulatory role to regulates genes in cis. Some of the major comments that needs to be addressed to strengthen the manuscript conclusions

1. One of the important controls could be targeting different or older L1s to show how it can affect gene expression. can authors perturb older families?
2. Although meta-analysis of L1s show up/downregulation of L1MdTf, ChIPseq for dCAS9 is needed to demonstrate which L1s are directly targeted in the experiment and analyse the data separately for dCAS9 bound L1s vs rest of the L1s in the subfamily.
3. L1s' transcriptional activation could be independent of their cis-regulatory activity. So, it is important to analyse the enhancer chromatin feature of TEs: Do they make 3D contact with the nearby genes?
4. how many replicates of RNA seq is done?
5. Are genes that respond to CRISPR activation in the same TAD? Do they loop with LINE1?
6. Figures 4 A &B show clear perturbation of host genes upon CRISPRi. However, they need to show L1s outside the genes (not in the introns) as CRISPR dCAS9 perturbation of Intronic L1s is expected to affect the expression of genes.
7. One of the key experiment missing is to genetically delete candidate L1s that are intergenic that are predicted to have a cis-regulatory function in the RNAseq data.
8. Authors should present the RNAseq data for genes 10 to 100 kb away from dCAS9-KRAB and dCAS9-VPR targeted L1s. It will be interesting to compare KRAB v VPR effect with distance.
9. The suggested role of L1s in neuronal gene expression is not strongly supported by their experiments or anlaysis. The authors end the results section with "Most of these genes are not expressed or have low expression levels in ESCs compared to other upregulated genes that are not part of these processes and pathways (Fig.S9E)". This result suggests that dCAS9-VPR targeting to multiple (How many are targeted is missing) L1s leads to the activation of many genes that are not normally expressed in mESCs due to the spreading of transcriptional activators or mESCs getting spontaneously differentiated to the neuronal lineage. Authors need to address these points.

Minor comments

Fig 2E) which housekeeping gene

Figures 4 A &B, show if these L1s make looping interactions or are in the same TAD as target genes.

Referee Cross-commenting

I agree with the other two reviewers points.

Significance

This study can be improved by further analysis or experimentation. In its current version, the conceptual advance offered by the current results and approach of the manuscript seem limited.

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Referee #2

Evidence, reproducibility and clarity

In this study Pérez-Rico et al. set out to study the cis-regulatory effects of evolutionary young L1 elements (specifically L1MdTf) in mouse embryonic stem cells. Using state of the art systems, they manage to silence/activate these elements expression and study the following gene expression cascade.

Major comments:

1. A general assessment or profiling of the L1MdTf expression in WT mESC is missing. It is very challenging to set their results in perspective (especially those of the repression system) without a general overview of the baseline L1-expression in mESC. How many elements does the WT mESC express? How is the genomic distribution of these elements? And how does it relate to nearby gene expression?
2. Off-target effects are very poorly documented and limited to in silico analysis. Documentation of changes in H3K4me3 and H3K9me3 upon activation/silencing would be beneficial to interpret the results. As it is now it is very difficult to understand why the activation-system is so much stronger that the silencing system.
3. It would be beneficial to explain why different experimental strategies were used for silencing/activation?
4. The study would benefit of a more detailed characterization of their systems' effect. E.g. It is not clear from Figure 3D-E how many of these repeats are part of the L1MdTf subfamily or other closely related subfamilies. This is relevant to assess the specificity of the systems.
5. The RNA-seq analysis relies on reads that are too short to uniquely map most L1s in the mouse genome. This should be mentioned and discussed.
6. A key issue that remains unresolved is the functional of L1-silencing/activation in mESC. Does this change cell morphology, pluripotency, or differentiation potential? This is essential information.
7. Fig 3B: Is this n=2? Hence why there is no statistical analyses? Same for Fig 5A-B: here a p-value is presented but it would be good to highlight the statistically significant results somehow.
8. Are only L1MdTf elements plotted in Fig 3D and 3E? As the authors claim that the system is quite specific, it would be good to have a clear view of the repeats that are differentially expressed and are evolutionarily close to the L1MdTf family. The figure might also benefit of some further characterization on a family level (multi-mapping) rather than single elements (unique mapping or multi mapping with reads that map to a single location, like here)
9. The authors provide some evidence for the existence of a bidirectional promoter on L1MdTf elements. In what elements was this observed? Does it result in chimeric transcripts? And if so, are these genes in line with the enrichment found?

Minor comments:

1. The introduction would benefit from a more detailed description of the L1-content in the mouse genome including the presence of polymorphic elements.
2. There is no characterization of the edited mESC. Stainings? Markers from bulk RNA seq analysis? Morphology assessment?

Significance

The manuscript is timely and in line to some similar and very recent studies suggesting a link between evolutionary young L1s and neuronal-related genes in mice (e.g. Toda et al.). However, the manuscript is quite preliminary in the current form. The investigation of potential off-target effects of their system requires more in-depth investigations. In addition, the manuscript could be improved with further exploration into the functional consequences of L1-silencing/activation.

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Referee #1

Evidence, reproducibility and clarity

Summary

The authors utilize engineered transcriptional effectors (CRISPRa or KRAB-Zinc Finger proteins) to activate or inhibit the expression of retrotransposons in mouse embryonic stem cells. They focus on a young L1 family in mouse, L1MdTf, which is particularly active. This study reveals extensive alterations in gene expression for surrounding genes, and it suggests that the dysregulated genes are enriched in repressive chromatin and preferentially associated with neuronal functions.

Major comments

The experiments are well-executed and controlled overall. However, to fully support the conclusions, a few aspects of the work could be strengthened:

1. Engineered Effector Binding: The binding sites for the engineered effectors (CRISPRa or KRAB-Zinc Finger proteins) were predicted computationally, but not validated experimentally using techniques like ChIP-seq. Although mapping reads within L1MdTf might be challenging, ChIP-seq could still be informative. It would help define the ratio of on-target vs. off-target binding and elucidate potential off-target effects (binding outside L1MdTf repeats).
2. Mechanism of action: The study somehow assumes that the effectors influence L1MdTf transcription, which then impacts the host transcriptome. However, it is also possible that the engineered effectors directly modulate nearby cis-regulatory elements (promoters or enhancers) due to their proximity to L1MdTf sequences. Further investigation is needed to differentiate between these possibilities.
3. Statistics: The study lacks robust statistical testing in several figures (e.g., Fig. 1B,D; 2C,E; S2; S5C,D). Additionally, the null hypotheses and statistical models used are not explicitly defined. To strengthen the analysis, the authors could quantify the percentage of differentially expressed (DE) or allele-specifically expressed genes associated with targeted L1s compared to non-targeted L1s or other relevant control groups. Furthermore, neuronal genes are known to be longer than average, which can bias enrichment analyses like those performed using DAVID. This increased length makes them more likely to harbor L1 insertions and potentially be affected by the engineered effectors targeting these elements. It would be informative to see how the conclusions change if the null models account for gene size or only consider genes with full-length L1MdTf elements.
4. Allele-specific expression: The analysis of allele-specific expression could be further strengthened by incorporating L1 heterozygosity data. Since the whole genome sequence of these cells is available, calling genotypes for L1 insertions using established pipelines like MELT or others would be a straightforward approach. This would allow the authors to ensure that allele-specific expression patterns are indeed associated with L1 insertional polymorphisms.

Minor comments

1. Western blot analysis could benefit from a more quantitative approach. Analyzing the intensity profiles of the ORF1p bands might help differentiate between potential ORF1p isoforms and pinpoint the specific changes (reduction or increase) in the top band. Additionally, an earlier explanation for the observed doublet band as a consequence of coexisting L1 families would be helpful for readers unfamiliar with mouse L1s.
2. The chromHMM enrichment analysis reports fold enrichments (ratios of observed vs. expected associations with chromatin states). However, the magnitude of these enrichments seems to be modest in most cases. It would be informative to see the actual number of sequences falling into each category for a better understanding of the enrichment patterns.

Significance

Strengths

• This study contributes to a limited body of research exploring the consequences of the global activation or repression of entire transposable element families.
• Notably, the authors achieve this manipulation in a relevant cell type (embryonic stem cells) where retrotransposition is known to occur, utilizing a retrotransposition-competent L1 family (L1MdTf).

Limitations

• While the study offers a relatively novel approach, the biological question addressed could be further refined. This would allow for more specific conclusions regarding the role/consequences of L1MdTf dysregulation.
• Artificially targeting L1 sequences is conceptually similar with randomly targeting the genome for transcriptional effects, since many, possibly most, L1 elements may not be naturally expressed under any biological conditions.

While the manuscript confirms the known potential of L1 sequences to act as cis-regulatory elements, it does not provide significant new insights into the mechanisms underlying their regulatory potential. Notably, a recent study by Tong et al. IJMS (2024) demonstrated the activation of young human L1 elements using CRISPRa. This work similarly confirmed the ability of young human L1 elements to form chimeric transcripts and influence gene expression, likely through promoter or enhancer activity. However, key limitations of both studies are that the strength of the engineered effector might influence the observed transcriptional effects, and that the targeted L1 elements might not be naturally expressed, potentially leading to an overestimation of the regulatory impact of L1 activation.

The study focuses on the impact of L1MdTf on gene expression, but exploring the phenotypic consequences of manipulating its expression could significantly broaden its significance. This would provide valuable insights into the functional impact of L1 activity in a broader context, potentially attracting a wider audience. In this context, L1MdTf silencing in mESC cells which naturally express these elements could be more insightful than artificially over-activating them. Phenotypic analyses could encompass cell cycle progression, commitment to the primed pluripotent state, totipotency, differentiation potential, DNA damage response, or X chromosome inactivation. Identifying whether observed phenotypes arise from cis-effects (on neighboring genes) or trans-effects (mediated by L1 RNA or proteins) would be crucial for understanding the underlying mechanisms.

My field of expertise lies in molecular and cellular biology and genomics, with a particular focus on transposable elements.

Reviewer #2 (Public review):

In this study, Xu et al. investigated the regulatory mechanisms controlling intramolecular cleavage of the transmembrane transcription factor MYRF-1, an important event that controls developmental progression in C. elegans.

The authors made important advances in several aspects:

(1) Through endogenous gene editing/tagging, further supported by western blots, the authors convincingly demonstrate the novel finding that the intramolecular cleavage and nuclear translocation of MYRF-1 is not static, but temporally controlled within each developmental stage: with nuclear translocation peaking at the late stage and then declining into lethargus/molts between developmental stages (Figure 1).

(2) They demonstrate that this cleavage and nuclear translocation is controlled by external stimuli, namely starvation.

(3) They reveal modes of regulation of the intramolecular cleavage that is mildly regulated by MYRF-1's own JM domain as well as the CCT tail of interacting partner PAN-1.

The conclusions of this paper are mostly well supported by data, but some aspects of the manuscript and conclusions should be clarified and extended to strengthen its findings.

(1) The authors concluded that the intramolecular cleavage and nuclear localization of MYRF-1 were similarly temporally-regulated in all tissue types. However, the data/image presented was limited to specific regions/cell types that were inconsistently chosen across developmental windows. For example, for the cleavage/nuclear translocation across L1 into lethargus (Figures 1B, E, F, G), the heads of the worm were shown to comprise mostly neurons and muscles. While across the rest of the larval stages, only mid-body pictures were shown, comprising mostly hypodermal and some intestinal cells. A complete coverage of all tissues across all time points would better support the author's conclusion that this temporal regulation occurs similarly in all tissue types. Additionally, the authors should clearly indicate which tissue/cell-types were used in the quantifications, as these were not done for several figure panels (including but not limited to Figure 1I and J).

(2) Related to point 1 above, this inconsistency in tissue assessment was also true for downstream experiments (Figures 2-6; e.g., starvation, JM, and CCT regulation, etc.). Broad tissue specific assessment for all downstream experiments would greatly enhance the strength and relevance of the findings. Judging by the current data presented (Figures 3, 5, 6), it seems to suggest that there are tissue/cell-type differences in the regulation of MYRF-1 nuclear translocation.

(3) Developmental progression was superficially and inconsistently assessed across the study. Developmental progression was mainly assessed by hypodermal (V-lineage) division patterns and worm length in this study. Several glaring omissions that should have been examined were the lengths of larval stages/lethargus and molting defects, as well as gonad development, to help identify which developmental landmarks were affected vs. not.

(4) The phosphorylation within MYRF-1's JM domain was insufficiently investigated. There were two serine phosphorylation sites that were discovered through mass spectrometry experiments, however the authors only investigated one of the serine (S623) residues without any justifications for the choice. Additional investigation of the other residues, as well as both together, would strengthen the relevance of these phosphorylation events to cleavage and nuclear translocation, especially considering the minimal effect observed with only mutating the one residue.

Reviewer #3 (Public review):

Summary:

In this paper, the authors identified dual inhibitory mechanisms, an intrinsic juxtamembrane (JM) region and an extrinsic cytoplasmic tail (CCT) domain in the binding protein PAN-1, that suppress MYRF-1 cleavage in C. elegans. The authors showed that MYRF-1 cleavage oscillates across larval stages, peaking in mid-to-late phases and being suppressed during molts. This oscillatory pattern is consistent with MYRF-1's role in promoting transitions of larval stages, particularly in late-L1 involving lin-4 activation and DD neuron remodeling.

Strengths:

This work generated several knock-in strains of fluorescent tags and mutations in the endogenous myrf-1 and pan-1gene loci, which will provide resources for future identification and characterization of the underlying molecular mechanisms regulating MYRF-1 cleavage inhibition.

The results presented in the paper are solid enough to support the paper's main conclusions.

This study is valuable for establishing MYRF-1 cleavage as a key gatekeeper of the C. elegans developmental timing. Findings from C. elegans MYRF-1 may provide insight into the regulation and function of mammalian MYRF.

Weaknesses:

The following points should be discussed to further support the authors' model that MYRF-1 cleavage is a key gatekeeper of developmental timing.

(1) Recent findings by Helge Großhans and Jordan Ward groups showed that KIN-20 (CK1δ) and LIN-42 (PERIOD) are required for proper molt timing in C. elegans, and that loss of LIN-42 binding or of the phosphorylated LIN-42 tail impairs nuclear accumulation of KIN-20, resulting in arrhythmic molts (EMBO J. 44, 6368-6396, 2025). In this paper, the authors concluded that PAN-1 promotes MYRF trafficking to the cell membrane, where MYRF-1 cleavage and nuclear translocation occur, and that oscillates with developmental molting cycles in C. elegans. It is unclear whether MYRF-1 and KIN-20 interact in the nucleus and, if so, how this interaction controls developmental timing.

(2) Separately, it was previously shown that the let-7 primary transcript (pri-let-7) exhibits oscillating, pulse-like expression that peaks during each larval stage, rather than a steady increase, and directly correlates with developmental molting cycles. It is unclear whether the nuclear-localized MYRF-1 fragment regulates the oscillatory primary let-7 expression during larval transition (McCulloch and Rougvie, 2014; Van Wynsberghe et al., 2011).

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Feng et al. uses mouse models to study the embryonic origins of HSPCs. Using multiple types of genetic lineage tracing, the authors aimed to identify whether BM-resident endothelial cells retain hematopoietic capacity in adult organisms. Through an important mix of various labeling methodologies (and various controls), they reach the conclusion that BM endothelial cells contribute up to 3% of hematopoietic cells in young mice.

Strengths:

The major strength of the paper lies in the combination of various labeling strategies, including multiple Cdh5-CreER transgenic lines, different CreER lines (col1a2), and different reporters (ZsGreen, mTmG), including a barcoding-type reporter (PolyLox). This makes it highly unlikely that the results are driven by a rare artifact due to one random Cre line or one leaky reporter. The transplantation control (where the authors show no labeling of transplanted LSKs from the Cdh5 model) is also very supportive of their conclusions.

We appreciate the Reviewer’s consideration of the strengths of our study supporting the identification of adult endothelial to hematopoietic transition (EHT) in the mouse bone marrow.

Weaknesses:

We believe that the work of ruling out alternative hypotheses, though initiated, was left incomplete. We specifically think that the authors need to properly consider whether there is specific, sparse labeling of HSPCs (in their native, non-transplant, model, in young animals). Polylox experiments, though an exciting addition, are also incomplete without additional controls. Some additional killer experiments are suggested.

Recognizing the importance of the weaknesses pointed by the Reviewer, we provide below our response to the thoughtful recommendations rendered.

Reviewer #1 (Recommendations for the authors):

The main model is to label cells using Cdh5 (VE-cadherin) CreERT2 genetic tracing. Cdh5 is a typical marker of endothelial cells. The data shows that, when treating adults with tamoxifen, the model labels PBMCs after ~10 days, and the labeling kinetics plateau by day 14... The authors reach the main conclusion: that adult ECs are making hematopoietic cells.

We agree that the main tool used in this study is to label endothelial cells (ECs) using Cdh5 (VE-Cadherin) CreERT2 genetic tracing in mice. Indeed, Cdh5 is recognized as a good marker of ECs. As a minor point, we wish to clarify that the results from treating adult Cdh5-CreERT2 mice with tamoxifen (Figure 1F) show that the ZsGreen labeling kinetics plateau by day 28 (not by day 14).

Important controls should be shown to rule out alternative possibilities: namely, that the CreERT2 reporter is being sparsely expressed in HSPCs. Many markers, specific as they may seem to be, can show expression in non-specific lineages - particularly in the cases of BAC and PAC transgenic models, in which the transgene can be present in multiple tandem copies and subject to genome location-specific effects. As the authors remind readers, the Cdh5 gene is partly transcribed (though at low levels) in HSPCs, and even more clearly expressed in specific subpopulations such as CLPs, DCs, pDCs, B cells, etc. Some options would be to: i) check if the Cdh5-CreERT2 transgene (not endogenous Cdh5, but the BAC/PAC transgene) is expressed in LSKs (at least by qPCR), ii) verify if any CreERT2 protein levels are present in LSKs (e.g., by western blot), and iii) check if tamoxifen is labeling any HSPCs freshly after induction (e.g., flow cytometry data of ZsGreen LSKs at 24-48h post tamoxifen injection).

We fully agree with the Reviewer that many markers, allegedly specific to a certain cell type, can show expression in other cell lineages. We also agree that excluding sparse or ectopic CreERT2 expression in hematopoietic stem and progenitor cells (HSPCs) is essential for interpreting lineage-tracing results. As suggested by the Reviewer, we have now examined if the Cdh5-CreERT2 transgene is expressed in bone marrow LSKs. To this end, we analyzed the Polylox single-cell RNAseq dataset presented in this study, containing ZsGreen⁺ ECs and enriched ZsGreen⁺ LSKs. As shown in the revised Figure S4D, CreERT2 transcripts were detected exclusively in Cdh5-expressing endothelial populations and were absent from Ptprc/CD45-expressing hematopoietic cells, except for plasmacytoid dendritic cells (pDCs; Figure S4E). These results are consistent with the RNAseq data from adult mouse bone marrow[1] showing that the Cdh5 gene is not expressed in HSPCs, CLPs, DCs, or B cells. Rather, among hematopoietic CD45⁺ cells, Cdh5 is only expressed in a small subset of plasmacytoid dendritic cells (pDCs), which are terminally differentiated cells. These published results are described in the text.

To further support this conclusion, we provide additional single-cell RNAseq analyses from our unpublished dataset of LSKs isolated from Cdh5-CreERT2/ZsGreen mice and not enriched for ZsGreen expression. These new analyses were performed after integrating the single-cell data from ECs and ZsGreen⁺ hematopoietic cells from the Polylox dataset (current study). As shown in Author response images 1 and 2, CreERT2 expression closely matches the expression patterns of Cdh5, Pecam1, and Emcn and is not detected in Ptprc/CD45-expressing hematopoietic cells.

Author response image 1.

Expression of CreERT2, Cdh5, Ptprc and ZsGreen in BM cell populations enriched with ECs and hematopoietic cells. The single-cell RNAseq results are derived from ZsGreen-enriched BM ECs and ZsGreen-enriched BM hematopoietic cells were derived from Polylox lineage-tracing experiments (data shown in Fig. 5; 37,667 ECs and 48,065 BM hematopoietic cells) and from LSKs (23,017 cells) independently isolated from tamoxifen-treated Cdh5-CreERT2/ZsGreen mice without ZsGreen enrichment (unpublished data).

Author response image 2.

Expression of CreERT2, Cdh5, Ptprc, Pecam1, Emcn, ZsGreen1, Col1a2, Cd19, Cd3e, Itgam (CD11b), Ly6a (Sca-1), Kit(cKit), Cd34, Cd48, Slamf1 (CD150), and Siglech in enriched BM ECs and LSKs from Cdh5-CreERT2/ZsGreen mice treated with tamoxifen 4 weeks prior to harvest (same cell source as indicated in Author response image 1).

Additionally, we functionally tested whether hematopoietic progenitors could acquire ZsGreen labeling following tamoxifen administration using transplantation assays (Figure 4A-D). ZsGreen^- LSKs (purity 99%), sorted from Cdh5-CreERT2/ZsGreen donors that had never been exposed to tamoxifen to exclude background Cre leakiness, were transplanted into lethally irradiated wild-type recipients. After stable hematopoietic reconstitution, recipients were treated with tamoxifen. If transplanted HSPCs or their progeny expressed CreERT2, tamoxifen administration would be expected to induce ZsGreen labeling. However, no ZsGreen⁺ hematopoietic cells were detected in these recipients, demonstrating that hematopoietic progenitors from Cdh5-CreERT2/ZsGreen and their descendants do not undergo tamoxifen-induced recombination.

Together, the single-cell transcriptional and transplantation data demonstrate that CreERT2 expression and tamoxifen-induced recombination are restricted to Cdh5-expressing ECs (except for pDCs). These findings support the conclusion that ZsGreen⁺ hematopoietic cells arise from adult bone marrow ECs rather than from contaminating hematopoietic progenitors.

One important missing experiment is to trace how ECs actually do this hematopoietic conversion: meaning, which populations of HSPCs are being produced by adult ECs in the first instance? LT-HSCs? ST-HSCs? MPPs? GMPs? All of the above? What are the kinetics? Differentiation is likely to follow a hierarchical path, but this is unclear at the moment.

We agree that defining the earliest EC-derived hematopoietic cell progenitors and the kinetics by which these progenitors appear (LT-HSC vs ST-HSC/MPP vs lineage-restricted progenitors) would provide important insights into adult EHT.

In the current genetic labeling system, a rigorous kinetic analysis of hematopoietic cells first generated by EC-derived in vivo is not straightforward. Specifically, the low-level baseline reporter ZsGreen⁺ fluorescence in hematopoietic cells (dependent on EHT occurring prenatally, perinatally or in young mice or other causes (Figure 1 A-D and Figure S1 D-I) impairs identification of newly generated ZsGreen⁺ progenitors at early time points and distinguish them from baseline fluorescence. A potential solution might be to introduce serial harvests across multiple time-points in large mouse cohorts to capture rare transitional events with statistical significance.

We wish to emphasize that the primary objective of this study was to establish whether adult bone marrow ECs have a hemogenic potential. Our data demonstrate adult EC-derived hematopoietic cell output that includes progenitor-containing fractions and multilineage mature progeny, under both steady-state conditions. We acknowledge that the current work does not resolve the order and kinetics of hematopoietic cell emergence following EHT. Therefore, under “Limitations of the study” we explicitly state this limitation and frame the identification of the earliest endothelial-derived progenitors and their kinetics as an important direction for future work.

One warning sign is how rare the reported phenomenon is. Even when labeling almost 90% of the BM ECs, these make at most ~3% of blood (less than 1% in the transplants in Figure 4F, less than 0.5% in the col1a2 tracing in Figure 7). This means this is a very rare and/or transient phenomenon... The most major warning sign is the fast kinetics of labeling and the fast plateau. We know that: a) differentiation typically follows some hierarchy, b) in situ dynamics of blood production are slow (work by Rodewald and Höfer). Considering how fast these populations need to be replaced to reach a steady state so rapidly (as reported here, 2-4 weeks), the presumably specialized ECs would need to be steadily dividing and producing hematopoietic cells at a fast pace (as a side prediction, the adult "EHT" cluster would likely be highly Mki67+). More importantly, the ZsGreen LSKs produced by the ECs would have to undergo VERY rapid differentiation (much faster than normal LSKs) or otherwise, if 3% of them are produced by a top compartment (the BM ECs) every 4 weeks, then the labeled population would continue to grow with time. The authors could try to challenge this by testing if the ZsGreen LSKs undergo much faster differentiation kinetics or lower self-renewal (which does not seem to be the case, at least in their own transplantation data). We believe a more likely explanation is that the label is being acquired more or less non-specifically, directly across a bunch of HSPC populations.

The Reviewer correctly notes that that the population of hemogenic ECs in the adult mouse bone marrow is small and the output of hematopoietic cells from these hemogenic ECs accounts for at most 3% of blood cells. We agree that delineating the kinetics by which hematopoietic cells are generated from adult EC is important, as this information would provide important insights into adult EHT.

Nonetheless, we believe that the rapid appearance and early plateau of labeled blood cells in our experiments may not derive from a sustained, high-rate generation of labeled blood cells from self-renewing top-tier hematopoietic cell compartments, such as LT-HSCs. Rather, our data are more consistent with a predominantly lineage-restricted and biased hematopoietic progenitor cell population being the source of labeled blood cells. Supporting this interpretation, longitudinal analysis of peripheral blood shows that EGFP⁺ PBMCs are consistently enriched with myeloid cells, whereas EGFP^- PBMCs are predominantly B cells (Figure 4G and H). This myeloid lineage skewing is stable over time and contrasts with what would be expected if labeling were acquired broadly and nonspecifically across the hematopoietic hierarchy. Therefore, our results are more consistent with myeloid biased progenitors being among the first populations that EHT generates.

We acknowledge that our studies do not identify the earliest endothelial-derived hematopoietic cells produced in vivo, and do not define their differentiation kinetics. Addressing rigorously these questions would require temporally resolved lineage tracing with sufficiently powered cohorts at early time point to statistically distinguish from baseline reporter background. These important experiments were beyond the scope of the present study. As noted above, under “Limitations of the study” we explicitly state this limitation and frame the identification of the earliest endothelial-derived progenitors and their kinetics as an important direction for future work.

Transplant experiments in Figure 4 do offer a crucial experiment in support of the main conclusion of the manuscript. These experiments show that transplanted LSKs bearing the Cdh5-CreERT2 and ZsGreen reporter cannot acquire the tamoxifen-induced label post-transplantation - suggesting that the label is coming from ECs. However, it is also possible that the LSK Cdh5-CreERT expression is partly during the transplantation process... Indeed, we know through the aging data that the labeling is less active in aged mice. In any case, this would be verified by qPCR/western-blot (comparing native vs post-transplant LSKs).

We agree with the Reviewer that the experiment in Figure 4A-D “offer a crucial experiment in support of the main conclusion of the manuscript.” The results of this experiment show that ZsGreen negative LSKs from the Cdh5-CreERT2-ZsGreen reporter mice do not acquire tamoxifen-induced ZsGreen fluorescence post transplantation, supporting the endothelial cell origin of blood ZsGreen⁺cells.

The Reviewer raises the possibility a “that the LSK Cdh5-CreERT expression is partly during the transplantation process... , and that this Cdh5-CreERT expression may occur slowly as learned “through the aging data that the labeling is less active in aged mice.” As we show in Figure 3F, tamoxifen administration induced a similar percentage of ZsGreen⁺ECs in the bone marrow of Cdh5-Cre^ERT2(BAC)/ZsGreen mice, whether tamoxifen was administered to 6-week-old, 16-week-old, 26-week-old or 36-week-old mice. Similar results with Cdh5-CreERT2 (BAC) mice are reported in the literature[2]. Since the mice transplanted with ZsGreen^- LSKs were followed for 25 weeks after tamoxifen administration, we believe that the results in Figure 4A-D address the concern raised by the Reviewer.

Supporting the conclusion that LSKs from the Cdh5-CreERT2-ZsGreen reporter mice do not express the Cdh5-CreERT2 under a native -non-transplant- setting, we now provide transcriptomic data from Cdh5-CreERT2/ZsGreen mice (not transplanted) showing that CreERT2 expression closely tracks with expression of canonical endothelial markers (Cdh5, Pecam1, Emcn) and is not detectable in Ptprc/CD45-expressing hematopoietic cells (Author response images 1 and 2). These data were obtained from non-transplanted mice treated with tamoxifen at ~12 weeks of age and analyzed four weeks later. Together, these results indicate that CreERT2 expression is endothelial-restricted in Cdh5-CreERT2-ZsGreen reporter mice.

Figure 5 presents PolyLox experiments to challenge whether adult ECs produce hematopoietic cells through in situ barcoding. Several important details of the experiment are missing in the main text (how many cells were labeled, at which time point, how long after induction were the cells sampled, how many bones/BM-cells were used for the sample preparation, what was the sampling rate per population after sorting, how many total barcodes were detected per population, how many were discarded/kept, what was the clone-size/abundance per compartment). As presented, the authors imply that 31 out of ~200 EC barcodes are shared with hematopoietic cells... This would suggest that ~15% of endothelial cells are producing hematopoietic cells at steady state. This does not align well with the rarity of the behavior and the steady state kinetics (unless any BM EC could stochastically produce hematopoietic cells every couple of weeks, or if the clonality of the BM EC compartment would be drastically reduced during the pulse-chase overlap with mesenchymal cells. Important controls are missing, such as what would be the overlap with a population that is known to be phylogenetically unrelated (e.g., how many of these barcodes would be found by random chance at this same Pgen cut-off in a second induced mouse). Also, the Pgen value could be plotted directly to see whether the clones with more overlapping populations/cells (3HG, 127, 125, CBA) also have a higher Pgen. We posit that there are large numbers of hematopoietic clones that contribute to adult hematopoiesis (anywhere from 2,000-20,000 clones would be producing granulocytes after 16 weeks post chase), and it would be easy to find clones that overlap with granulocytes (the most abundant and easily sampled population) - HSPCs would be the more stringent metric.

We thank the Reviewer for highlighting the need for a more detailed description of the Polylox experiments. To address this deficiency, we have compiled a document (Additional Supplementary Information file) containing all the specifics of the Polylox experimental and analytical parameters in one location. This includes: (i) the number of cells analyzed per population, (ii) the time points of induction and sample collection, (iii) the number of bones and total bone marrow cells used for preparation, (iv) the sampling rate following cell sorting, (v) the total number of detected barcodes per population, (vi) barcode filtering criteria and numbers retained or discarded, and (vii) clone-size and barcode number across cell compartments. We have updated the manuscript to refer readers to this Supplementary file.

The Reviewer concluded from our results (Figure 5, Figure S5) that 31 out of ~200 endothelial cell (EC) barcodes shared with hematopoietic cells (HCs), implying that ~15% of ECs produce hematopoietic cell progeny at steady state. This interpretation in inconsistent with our data showing the rare nature of adult EHT and would require either that a large fraction of bone-marrow ECs can generate hematopoietic cells within short time windows, or that EC would clonally expand rapidly during the pulse-chase period, as noted by the Reviewer. The explanation for this apparent problem is technical. Briefly, the ~200 EC barcodes recovered do not represent all barcoded ECs. During Polylox barcode library construction, a mandatory size-selection step is applied prior to PacBio sequencing, retaining fragments that are approximately 800–1500 bp in length, whereas the full Polylox cassette spans ~2800 bp. This is mainly because the PacBio sequencer requires that the library be either 800-1500bp or over 2500bp, for optimal sequencing results. As described in the original Polylox publication[3,4], this size selection eliminates most (approximately 75%) longer barcodes, together with ~85% of the shorter barcodes. Thus, ECs harboring very long or short recombined barcodes are under-represented or excluded from sequencing. As a result, the 22 true barcodes linking ECs and HCs recovered from sequencing do not indicate that ~10–15% of ECs generate hematopoietic progeny. Rather, these barcodes represent a highly selected subset of ECs with barcode configurations compatible with library recovery and sequencing. The observed EC–HC barcode sharing thus reflects qualitative lineage connectivity, not the quantitative frequency of endothelial-derived hematopoiesis at steady state.

The Reviewer correctly notes that true Polylox barcodes are shared by ECs and mesenchymal-type cells and asks that we examine whether this overlap could occur by chance alone. The Polylox filtering threshold (pGen < 1 × 10^-6), that we have revised for stringency (from pGen < 1 × 10^-4, without altering the essential results; new Figure S4 and revised Figure 5C-F) renders such overlap exceedingly unlikely. At this threshold, the expected number of random recombination events among 4,069 barcoded cells is approximately 0.004. Consequently, among the 87 mesenchymal cells identified here, fewer than 0.4 cells would be expected, to share a barcode with another cell by chance alone. Thus, the probability of recovering identical barcodes across unrelated lineages due to random recombination is vanishingly small, and the observed EC–mesenchymal barcode sharing substantially exceeds random expectation.

Related to this observation, the Reviewer correctly notes that the endothelial and mesenchymal cell lineages are phylogenetically unrelated. However, endothelial-to-mesenchymal cell transition (EndMT), the process by which normal ECs completely or partially lose their endothelial identity and acquire expression of mesenchymal markers, is a well-established process that occurs physiologically and in disease states (Simons M Curr Opin Physiol 2023). In the bone marrow, the occurrence of EndMT has been documented in patients with myelofibrosis, and the process affects the bone marrow microvasculature (Erba BG et al The Amer J Patholl 2017). Single-cell RNAseq of non-hematopoietic bone marrow cells has shown the existence of a rare population of ECs that co-expresses endothelial cell markers (Cdh5, Kdr, Emcm and others) and the mesenchymal cell markers, as shown in Figure 6E and F.

We fully agree with the Reviewer that given the large number of hematopoietic clones contributing to adult hematopoiesis -particularly granulocyte-producing clones- it may be relatively easy to detect barcode overlap with abundant mature populations, whereas overlap with HSPCs would represent a more stringent and informative metric of lineage relationships. The Polylox results presented here show the sharing of true barcodes between individual ECs and HSPC.

Reviewer #2 (Public review):

Summary:

Feng, Jing-Xin et al. studied the hemogenic capacity of the endothelial cells in the adult mouse bone marrow. Using Cdh5-CreERT2 in vivo inducible system, though rare, they characterized a subset of endothelial cells expressing hematopoietic markers that were transplantable. They suggested that the endothelial cells need the support of stromal cells to acquire blood-forming capacity ex vivo. These endothelial cells were transplantable and contributed to hematopoiesis with ca. 1% chimerism in a stress hematopoiesis condition (5-FU) and recruited to the peritoneal cavity upon Thioglycolate treatment. Ultimately, the authors detailed the blood lineage generation of the adult endothelial cells in a single cell fashion, suggesting a predominant HSPCs-independent blood formation by adult bone marrow endothelial cells, in addition to the discovery of Col1a2+ endothelial cells with blood-forming potential, corresponding to their high Runx1 expressing property.

The conclusion regarding the characterization of hematopoietic-related endothelial cells in adult bone marrow is well supported by data. However, the paper would be more convincing, if the function of the endothelial cells were characterized more rigorously.

We thank the Reviewer for the supportive comments about our study.

(1) Ex vivo culture of CD45-VE-Cadherin+ZsGreen EC cells generated CD45+ZsGreen+ hematopoietic cells. However, given that FACS sorting can never achieve 100% purity, there is a concern that hematopoietic cells might arise from the ones that got contaminated into the culture at the time of sorting. The sorting purity and time course analysis of ex vivo culture should be shown to exclude the possibility.

We agree that FACS sorting can never achieve 100% cell purity and that sorting purity is critical for interpreting the ex vivo culture experiments presented in our study. As requested by the Reviewer, we have now documented the purity of the sorted endothelial cell (EC) population used in the ex vivo culture experiments. The post-sort purity of CD45<sup->/sup>VE-cadherin⁺ZsGreen⁺ ECs was 96.5 %; this data is now shown in the revised Figure 2B (Post Sort Purity panel). This purity level is comparable to purity levels of sorted ECs shown in Figure S2I (94.5 %).

While we agree that a detailed time-course analysis of hematopoietic cell output from EC cultures could further strengthen the conclusion that bone marrow ECs can produce hematopoietic cells ex vivo, we wish to call attention to the additional critical control in the experiment shown in Figure 2B-D. In this experiment, we co-cultured CD45⁺ZsGreen⁺ hematopoietic cells from Cdh5-CreERT2/ZsGreen mice, rather than ECs, and examined if these hematopoietic cells could produce ZsGreen⁺ cell progeny after 8-week culture under the same conditions used in EC co-cultures (conditions not designed to support hematopoietic cells long-term). Unlike ECs, the CD45⁺ZsGreen⁺ hematopoietic cells did not generate ZsGreen⁺ hematopoietic cells at the end of the 8-week culture, indicating that the culture conditions are not permissive for the maintenance, proliferation and differentiation of hematopoietic cells. This provides strong evidence that even if few hematopoietic cells contaminated the sorted ECs, these hematopoietic cells would not contribute to EC-derived production of hematopoietic cells at the 8-week time-point. We have revised the text of the results describing the results of Figure 2B-D.

(2) Although it was mentioned in the text that the experimental mice survived up to 12 weeks after lethal irradiation and transplantation, the time-course kinetics of donor cell repopulation (>12 weeks) would add a precise and convincing evaluation. This would be absolutely needed as the chimerism kinetics can allow us to guess what repopulation they were (HSC versus progenitors). Moreover, data on either bone marrow chimerism assessing phenotypic LT-HSC and/or secondary transplantation would dramatically strengthen the manuscript.

The original manuscript reported survival and engraftment up to 12 weeks post transplantation. The recipient mice have now been monitored for up to 10 months post transplantation. These extended survival and engraftment data are now included in the revised Figure 2I and J replacing the previous 10-week analyses.

We agree with the Reviewer that the time-course kinetics of donor cell repopulation would help define adult endothelial to hematopoietic transition (EHT) and the hematopoietic cell types produced by adult (EHT). We did not perform serial time-course sampling of peripheral blood beyond the 10-week and the 10-month time-points. Given that the recipient mice were lethally irradiated with increased susceptibility to infection, we sought to minimize repeated interventions that could compromise animal health and survival. We therefore prioritized long-term survival and endpoint analysis over repeated longitudinal sampling. Nonetheless, the long-term survival,10 months, and multilineage hematopoietic cell reconstitution after lethal irradiation provides functional evidence that adult EHT produced at least some LT-HSC.

We acknowledge that phenotypic assessment of bone marrow LT-HSC chimerism /or secondary transplantation would further strengthen the manuscript. We have clarified these limitations in the revised manuscript under “Limitations of the study”.

(3) The conclusion by the authors, which says "Adult EHT is independent of pre-existing hematopoietic cell progenitors", is not fully supported by the experimental evidence provided (Figure 4 and Figure S3). More recipients with ZsGreen+ LSK must be tested.

We agree with the Reviewer that, in most cases, a larger number of experimental data points is helpful to strengthen the conclusions, and that having additional mice transplanted with ZsGreen-enriched LSK would be desirable. However, we do not believe that additional mice transplanted with ZsGreen LSKs would strengthen the conclusions drawn from the experimental results shown in Figure 4D, in which we used 6 mice transplanted with ZsGreen-depleted (ZsGreen^-) LSKs and 2 mice transplanted with ZsGreen⁺-enriched (ZsGreen⁺) LSKs. The independence of adult EHT from “pre-existing hematopoietic cell progenitors” is based on the following experimental results and conclusion from these results.

First, ZsGreen^- LSKs (purity 99%) isolated from Cdh5-CreERT2/ZsGreen mice were transplanted into lethally irradiated WT recipients (n = 6). These ZsGreen^- LSKs robustly reconstituted hematopoiesis, demonstrating successful engraftment. Importantly, tamoxifen administration to the recipients of ZsGreen^- LSKs produced no detectable ZsGreen⁺ cells in the blood for up to 6 months post transplantation (Figure 4D, blue line encompassing the results of the 6 mice). This result demonstrates that the transplanted ZsGreen^- hematopoietic progenitors and their progeny do not acquire ZsGreen labeling in vivo following tamoxifen treatment, indicating that they lack the Cre-recombinase. This result is consistent with the endothelial specificity of Cdh5 expression.

Second, ZsGreen⁺ LSKs (accounting for ~50% of the LSKs) isolated from Cdh5-CreERT2/ZsGreen mice were transplanted into lethally irradiated WT recipients (n = 2). This arm of the experiment was performed in part as a technical control to confirm successful engraftment and detection of ZsGreen⁺ hematopoietic cells in the transplant setting. Importantly, tamoxifen administration to the two recipients of ZsGreen⁺ LSKs (Figure 4D, two green lines reflecting these two mice) show that the level of ZsGreen⁺ blood cells stabilized in each of the mice between week 10 and 24, showing equilibrium between the proportion of ZsGreen⁺ and ZsGreen^-cells in the blood. This indicates that pre-existing ZsGreen⁺ LSK are not responsible for tamoxifen-induced increases in ZsGreen⁺ hematopoietic cell in blood.

Together, the results from this experiment demonstrate that in the setting of transplantation, tamoxifen does not induce ZsGreen labeling of ZsGreen- hematopoietic progenitors/their progeny. This result strongly supports the conclusion that ZsGreen⁺ hematopoietic cells arise independently of pre-existing or inducible hematopoietic progenitors. We have revised the text to clarify these experiments and to present the results in a simplified manner.

Strengths:

The authors used multiple methods to characterize the blood-forming capacity of the genetically - and phenotypically - defined endothelial cells from several reporter mouse systems. The polylox barcoding method to trace the adult bone marrow endothelial cell contribution to hematopoiesis is a strong insight to estimate the lineage contribution.

Weaknesses:

It is unclear what the biological significance of the blood cells de novo generated from the adult bone marrow endothelial cells is. Moreover, since the frequency is very rare (<1% bone marrow and peripheral blood CD45+), more data regarding its identity (function, morphology, and markers) are needed to clearly exclude the possibility of contamination/mosaicism of the reporter mice system used.

We agree that the biological significance and functional roles of hematopoietic cells generated de novo from adult bone marrow ECs remain important open questions. We also agree that the output of hematopoietic cells from adult EHT is low, but rare events can be important, particularly as they pertain to stem/progenitor cell biology. Both points are described under “Limitations of the study”. The primary goal of the present study was to address the question whether adult bone marrow ECs can undergo EHT. We believe that the combination of various mouse transgenic lines, different Cre-ER, different reporters (ZsGreen and mTmG), including the s.c. barcoding reporter (PolyloxExpress), different approaches to evaluate hematopoiesis in vivo and ex vivo, makes it rather unlikely that our conclusions are driven by an artifact related to a specific leaky reporter, contamination, or problems with one of the Cre-lines. The experiment where we find no tamoxifen-induced labeling of transplanted ZsGreen^- LSKs derived from the Cdh5-CreERT2/ZsGreen mice is strongly supportive of the existence of adult EHT, virtually excluding a contribution of contaminant hematopoietic cells.

Reviewer 2 Recommendations for the authors:

(1) There is a discrepancy in the proportion of peripheral blood composition between different reporters (mTmG and ZsGreen) (Figure 1G and Figure S1K), especially the contrasting B cell proportion between both models. The additional comments on this data should be mentioned.

In the revised Results section, we now note that the mTmG and ZsGreen reporters show slightly different efficiencies or kinetics of labeling. These differences have previously been reported[5] and have been attributed to relative reporter leakiness, sensitivity to tamoxifen, or different kinetics of Cre recombination. As suggested, these comments have been added to the text following the description of (Figure S2A).

(2) Experimental methods concerning cell transplantation/transfer need more information, such as: a) using or not using rescue cells and how many cells are they if using, b) single or split dose of irradiation, c) when were cells transplanted following irradiation, etc. Otherwise, the data are uninterpretable.

We have ensured that the Material and Methods section under “Bone marrow ablation and transplantation” contains all the information requested by the Reviewer.

(3) Some of the grouped data haven't been statistically analyzed.

We have reviewed all data and performed appropriate statistical analyses where comparisons were made. In the revised figures and legends, all grouped datasets now include statistical tests and p-values are indicated (added to Fig. 3H and I; Figure 4G).

(4) Some flowcytometry plot has the quantitative number, others do not. The quantitative information is absolutely needed in all flow cytometry plots.

We have updated the flow cytometry figures to include quantitative values (percentages or absolute counts) in all relevant plots (2B (new figure, bottom left); 2C; S1G, S1H).

(5) It is more relevant to present the Emcn/VE-Cadherin plot from gated CD45+/ZsGreen+, not the CD45-/ZsGreen+ fraction (Figure 2C), as the latter were not the EHT-derived offspring, but rather the common phenotypic endothelial cells

As requested, we have added the suggested flow cytometry plot. The revised Figure 2C now includes an Emcn vs. VE-Cadherin plot from the gated CD45⁺ZsGreen⁺ population. This complements the existing panel and confirms that the cells of interest retain endothelial cell markers after culture, while the CD45⁺ZsGreen⁺ cells did not express endothelial markers. The figure legend has been updated to explain the new panel. We agree that this plot more directly highlights the phenotype of the presumed EHT-derived cells.

(6) To show the effect of the ex vivo culture, the authors should present the absolute number of CD45+ZsGreen+ cells in the pre-/post-culture; otherwise, the data are uninterpretable (Figure 2D).

Our interpretation of the Reviewer’s comment above (relative to the experiment shown in Figure 2B-D) is that the Reviewer would like that we provide the absolute number of CD45⁺ZsGreen⁺ cells introduced into the co-culture (supplemented with unsorted BM cells, ZsGreen⁺ hematopoietic cell or ZsGreen⁺ ECs) and the absolute number of CD45⁺ZsGreen⁺ cells recovered at the end of the 8-week culture. Currently, the results in Figure 2D show the absolute number of CD45⁺ZsGreen⁺ cells recovered at the end of the 8-week culture. The input of CD45⁺ZsGreen⁺ cells for unsorted BM cells was 2.93e6 on average; for ZsGreen⁺ hematopoietic cells was 1.68e6 on average and from sorted ZsGreen⁺ ECs was estimate up to 100.

(7) It is confusing to see Figures 2F and 2G, which apparently show the data from the middle of the experimental procedure (Figure 2E). Those data should be labelled clearly regarding which procedures of the whole experiment protocol.

As correctly noted by the Reviewer, Figures 2F and 2G provide data that relate to the middle of the graphical representation of the experiment shown in Figure 2E. We see how this may be confusing.

Therefore, we have updated both the figure labeling and legend to explicitly indicate that Figure 2F and 2G provide the FACS sorting results for the cells used for transplantation. The revised legend now reads: “Representative flow cytometry plots of the non-adherent cell fraction after 8 weeks of co-culture (cells used for transplantation).”

References

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(2) Identification of a clonally expanding haematopoietic compartment in bone marrow | The EMBO Journal | Springer Nature Link https://link.springer.com/article/10.1038/emboj.2012.308.

(3) Pei, W., Shang, F., Wang, X., Fanti, A.-K., Greco, A., Busch, K., Klapproth, K., Zhang, Q., Quedenau, C., Sauer, S., et al. (2020). Resolving Fates and Single-Cell Transcriptomes of Hematopoietic Stem Cell Clones by PolyloxExpress Barcoding. Cell Stem Cell 27, 383-395.e8. https://doi.org/10.1016/j.stem.2020.07.018.

(4) Pei, W., Feyerabend, T.B., Rössler, J., Wang, X., Postrach, D., Busch, K., Rode, I., Klapproth, K., Dietlein, N., Quedenau, C., et al. (2017). Polylox barcoding reveals haematopoietic stem cell fates realized in vivo. Nature 548, 456–460. https://doi.org/10.1038/nature23653.

(5) Álvarez-Aznar, A., Martínez-Corral, I., Daubel, N., Betsholtz, C., Mäkinen, T., and Gaengel, K. (2020). Tamoxifen-independent recombination of reporter genes limits lineage tracing and mosaic analysis using CreERT2 lines. Transgenic Res 29, 53–68. https://doi.org/10.1007/s11248-019-00177-8.

Le Pilotage Partagé et le Rôle Stratégique de la Vie Scolaire

Synthèse

Ce document analyse les mutations profondes de la Vie Scolaire au sein du système éducatif français, passant d'un service de gestion des flux et de la discipline à un levier stratégique de réussite.

Le Conseiller Principal d'Éducation (CPE) s'affirme désormais comme un cadre pivot, expert du climat scolaire et de la socialisation, dont l'action s'articule étroitement avec le pilotage pédagogique.

La réussite d'un établissement repose sur la transition d'une « Vie Scolaire qui gère » vers une « Vie Scolaire qui pilote », intégrée dans une dynamique de pilotage partagé fondée sur la confiance, la délégation réelle et la déconstruction de la frontière artificielle entre l'éducatif et le pédagogique.

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1. Perspectives Historiques et Mutation des Enjeux

L'évolution du système éducatif a transformé la Vie Scolaire en un point névralgique de l'établissement.

• L'héritage du collège unique : Depuis 50 ans, l'accueil de l'intégralité d'une génération a radicalement changé la donne par rapport au modèle historique qui ne scolarisait qu'une infime partie de la population.

• De la surveillance au pilotage : Historiquement centrée sur les « surveillants généraux » gérant ce qui se passait hors de la classe, la fonction a évolué vers le corps des CPE.

Cette mutation reconnaît l'importance du contexte de scolarisation (climat, santé mentale, inclusion) dans la réussite des apprentissages.

• La singularité française : Le CPE est une exception française issue de la séparation précoce entre la transmission des savoirs (domaine des enseignants) et les tâches d'encadrement, longtemps jugées moins légitimes par le corps professoral.

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2. Le CPE : Un Cadre Pivot et non un Exécutant

Le positionnement institutionnel du CPE est celui d'un cadre à part entière, dont les missions dépassent la simple application du règlement intérieur.

Un statut de cadre affirmé

Le CPE n'est pas un exécutant des décisions de la direction, mais un conseiller technique associé aux décisions éducatives et pédagogiques.

• Expertise des interstices : Le CPE agit dans les articulations du système, offrant une vision globale de l'élève.

• Responsabilité de service : Il dirige le service de Vie Scolaire (AED) et participe à l'élaboration de la politique éducative de l'établissement (circulaire de mission de 2015).

Les caractéristiques du métier

| Caractéristique | Impact sur le fonctionnement | | --- | --- | | Position d'entre-deux | Le CPE se situe à l'interface entre la direction, les enseignants, les élèves et les familles. | | Minorité numérique | Souvent seul ou en très petit nombre (1 à 5 par établissement), il doit déployer une intelligence collective pour agir sur une masse importante d'enseignants. | | Polyvalence | Il alterne entre la gestion de l'urgence (discipline, crises) et le travail de long terme (projets, engagement lycéen/collégien). |

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3. Déconstruire la Frontière Éducatif / Pédagogique

Le document souligne que la distinction entre l'éducatif (Vie Scolaire) et le pédagogique (Classe) est un « mythe républicain » de moins en moins pertinent.

• Interdépendance : Les modalités d'éducation participent directement à la qualité des apprentissages. Un élève ne peut apprendre correctement si le climat scolaire ou sa santé mentale est dégradé.

• Le Conseil Pédagogique : La présence du CPE dans cette instance est jugée symboliquement et stratégiquement essentielle.

Elle permet d'intégrer la vision éducative aux réflexions sur les apprentissages et vice versa.

• Projets communs : Le CPE devient un animateur de projets où les élèves sont acteurs (CVC, CVL), transformant la vie scolaire en un espace d'apprentissage de la citoyenneté.

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4. Les Clés du Pilotage Partagé

Le terme « équipe de direction élargie » est parfois jugé obsolète ou sémantiquement complexe ; les experts privilégient la notion de pilotage partagé.

Conditions de réussite du pilotage

• La Confiance : Elle est la condition sine qua non. Le chef d'établissement doit créer un écosystème où la parole est libre et les points de vue contraires acceptés.

• La Délégation Réelle : Déléguer signifie confier des dossiers entiers (et non des tâches) en octroyant une autonomie de décision et les moyens d'agir.

• L'Expertise Reconnue : Le CPE doit être sollicité pour son expertise technique lors de l'élaboration de l'ordre du jour des réunions de direction.

La métaphore du « vol en escadrille »

Plutôt qu'un modèle pyramidal où seul le pilote (chef d'établissement) décide, le pilotage partagé ressemble à un vol en escadrille :

• Chacun connaît sa place et sa mission.

• La configuration est agile et permet de réagir rapidement aux difficultés.

• Personne ne « vole seul », renforçant le sentiment d'appartenance à une communauté professionnelle.

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5. Rituels de Gouvernance et Outils Stratégiques

Pour éviter l'isolement de la Vie Scolaire, plusieurs dispositifs concrets sont préconisés :

• Le Comité de Direction (Codir) : Réunion hebdomadaire (souvent d'une durée de 2 heures) associant les cadres (Direction, CPE, Gestionnaire) pour définir la stratégie et suivre les dossiers.

• Le Projet de Service : Document qui définit les priorités de la Vie Scolaire en fonction du contexte local (urbain, rural, industriel), permettant de réguler la charge de travail et d'éviter le sentiment de « barque surchargée ».

• La Politique de la Porte Ouverte : Accessibilité mutuelle permanente entre le chef d'établissement et le CPE pour réguler les urgences et désamorcer les tensions.

• Comités de pilotage ciblés : Instances courtes et gratifiantes regroupant les acteurs responsables de dossiers spécifiques (harcèlement, décrochage, santé mentale).

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6. Nouveaux Défis : Santé Mentale et Engagement

Depuis la crise du Covid-19, de nouvelles problématiques ont émergé, renforçant le rôle de veille du CPE.

• Santé mentale : On observe une libération de la parole des élèves et une augmentation des situations de mal-être. Les services de Vie Scolaire sont les premiers réceptacles de cette détresse.

• Harcèlement (Programme Phare) : La formation accrue des personnels permet de briser les tabous et de passer d'une simple surveillance à un accompagnement global.

• Engagement des élèves : Le CPE doit « faire avec » les élèves et non « pour » eux, en les responsabilisant dans des instances comme le CVC ou le CVL pour garantir la pérennité des projets.

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Citations Clés

« On ne passe pas d'une vie scolaire qui gère à une vie scolaire qui pilote sans une équipe de direction réellement partagée. »

« Le CPE est le métier des interstices, des articulations, celui qui essaie de faire du lien. »

« La délégation, c'est garantir à chacun sa capacité d'agir. Ce n'est pas consulter, c'est confier la responsabilité. »

« La Vie Scolaire n'est pas une périphérie, c'est un cœur battant de l'établissement. »

1. What are some personal experiences you have that relate to larger social issues? I was a medical provider back home in Nepal. During rural rotation, I saw a pregnant woman walk up to 4 hours to reach a basic health check post and denied basic care because she did not have insurance and could not pay out of pocket.
2. Why are these issues important to you? This experience is important to me, it shows how even the most basic healthcare is inaccessible to people in Nepal. Irony is that Nepal's constitution guarantees basic access to health care to everyone. This moment forced me to question how if a pregnement woman walking 4 hours in labour can be denied care , what would be the fate of others facing serious issues.
3. Choose one of these issues to discuss: Why or how would your research of this issue represent an example of “intrinsic motivation” for you? Universal health care to basic medical care in Nepal: i would research this topic because that is one of the most basic need that a citizen would expect from their government. I want learn more on how my country is not able to provide basic acess to healthcare. Name: Kamal Shrestha

Reviewer #2 (Public review):

Summary:

This study addresses the hypothesis that the strikingly higher prevalence of autoimmune diseases in women could be the result of biased thymic generation or selection of TCR repertoires. The biological question is important and the hypothesis is valuable. Although the topic is conceptually interesting and the dataset is rich, the study has a number of major issues. In particular, the majority of "autoimmunity-related TCRs" considered in this study are in fact specific to type 1 diabetes (T1D). Notably, T1D incidence is higher in males, which directly contradicts the stated objective of the study - to explain the higher prevalence of autoimmune diseases in women. Given this conceptual inconsistency, the evidence presented does not support the authors' conclusions.

Strengths:

The key strength of this work is the newly generated dataset of TCR repertoires from sorted thymocyte subsets (DP and SP populations). This approach enables the authors to distinguish between biases in TCR generation (DP) and thymic selection (SP). Bulk TCR sequencing allows deeper repertoire coverage than single-cell approaches, which is valuable here, although the absence of TRA-TRB pairing and HLA context limits the interpretability of antigen specificity analyses. Importantly, this dataset represents a valuable community resource and should be openly deposited rather than being "available upon request."

Weaknesses:

I thank the authors for their detailed responses to my previous comments. Several concerns were addressed satisfactorily; however, important issues remain unresolved, and a new major concern has emerged from the revised manuscript.

Major concerns:

(1) Autoimmune specificity is dominated by T1D, contradicting the study's premise. Newly added supplementary Table 3 shows that the authors considered only 14 autoimmune-related epitopes, of which 12 are associated with type 1 diabetes (T1D) and 2 with celiac disease (CeD). (I guess this is because identification of particular peptide autoantigens is an extremely difficult task and was only successful in T1D and CeD.) Thus conclusions of this work mostly relate to T1D. However, the incidence of T1D is higher in males than in females (e.g. doi:10.1111/j.1365-2796.2007.01896.x; doi:10.25646/11439.2). This directly contradicts the stated objective of the study - to explain the higher prevalence of autoimmune diseases in women. As a result, the authors' conclusions (a) cannot be generalized to autoimmune disease as a whole as the authors only considered T1D and CeD antigens and (b) are internally inconsistent with the stated objective of the study.

(2) By contrast, CeD does show a female bias (~60/40 female/male; doi:10.1016/j.cgh.2018.11.013). However, the manuscript does not allow evaluation of how much the reported "autoimmune TCR enrichment" derives from T1D versus CeD. Despite my previous request, the authors did not provide per-donor and per-epitope distributions of autoimmune-specific TCR matches. I therefore explicitly request a table in which: each row corresponds to a specific autoimmune antigen; each column corresponds to a donor (with metadata available including sex); each cell reports the number of unique TCRs specific to that antigen in that donor. Without such data, the conclusions cannot be evaluated.

(3) It is scientifically inappropriate to generalize findings to "autoimmune diseases" when only T1D and CeD were analyzed. Moreover, given that T1D and CeD show opposite directions of sex bias, combining them into a single "AID" category is misleading. All analyses presented in Figure 8 and Supplementary Figure 16 should be repeated and shown separately for T1D and CeD, rather than combined.

(4) The McPAS database contains TCRs associated with other autoimmune diseases (e.g., multiple sclerosis, rheumatoid arthritis), although the exact autoantigens in these contexts are unknown. Why didn't the authors perform the search for such TCRs? I believe disease association even without particular known antigen could still be insightful.

(5) Misuse of the concept of polyspecificity. I appreciate the authors' reference to Don Mason's work; however, the concept of polyspecificity discussed there is fundamentally different from the authors' usage. Mason, Sewell (doi:10.1074/jbc.M111.289488), Garcia (doi:10.1016/j.cell.2014.03.047), and others demonstrated that individual TCRs can recognize multiple peptides, possibly around 1 million. But importantly these peptides are not random but share some sequence motif. This is a general feature of TCRs, i.e. 100% of TCRs are polyspecific in this sense.<br /> In contrast, the authors define polyspecificity as TRB sequences annotated as specific to unrelated epitopes in TCR databases such as VDJdb. These databases are well known to contain substantial numbers of false-positive annotations (see, e.g., Ton Schumacher's preprint https://www.biorxiv.org/content/10.1101/2025.04.28.651095.abstract). The authors acknowledge that, under their definition, polyspecificity has been experimentally validated for only one (!) TCR (Quiniou et al.). In the absence of robust experimental validation, use of the term "polyspecificity" in this context is misleading. I strongly recommend removing all analyses and conclusions related to polyspecificity from the manuscript unless supported by independent functional validation.

(6) I agree that comparing specificity enrichment between sexes is meaningful. However, enrichment relative to the database composition itself is not biologically interpretable, as acknowledged by the authors in their response. I therefore recommend removing Supplementary Figure 15, which is potentially misleading.

(7) In contrast, Supplementary Figure 16 represents the most convincing result of the study (keeping in mind that the AID group should be splitted to T1D and CeD with T1D and that T1D and CeD have opposing directions of sex biases) and should be shown as a main figure, replacing Figure 8A-B which is less convincing as it doesn't show per-donor distribution.

(8) The authors argue that applying mixed-effects modeling to Rényi entropy would require assuming a common sex effect across subsets. I do not find this assumption unreasonable. For example, if sex effects are mediated through AIRE-dependent negative selection, one would indeed expect a consistent direction of effect across subsets. The lack of statistical significance in Figure 3 may reflect limited sample size rather than true absence of the difference. Moreover, the title's phrasing "comparable TCR repertoire diversity" is vague: what is the statistical definition of "comparable"?

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This study provides useful insights into addressing the question of whether the prevalence of autoimmune disease could be driven by sex differences in the T cell receptor (TCR) repertoire, correlating with higher rates of autoimmune disease in females. The authors compare male and female TCR repertoires using bulk RNA sequencing, from sorted thymocyte subpopulations in pediatric and adult human thymuses; however, the results do not provide sufficient analytical rigor and incompletely support the central claims.

The statement in the editorial assessment that our study “does not provide sufficient analytical rigor” surprised us. TCR repertoire analysis is indeed a highly complex domain, both experimentally and computationally. We consider ourselves to be leading experts in this field and have invested a great deal of effort to ensure the rigor and reproducibility of every analytical step.

Specifically, our group has previously benchmarked and published validated methodologies for the following areas: (i) TCR repertoire generation (Barennes et al., Nat Biotechnol 2021), (ii) repertoire analysis (Six et al., Frontiers in Immunol, 2013; Chaara et al., Frontiers in Immunol, 2018; Ritvo et al., PNAS, 2018; Mhanna et al., Diabetes, 2021; Trück et al., eLife, 2021; Quiniou et al., eLife, 2023; Mhanna et al., Cell Rep Methods, 2024; Mhanna et al., Nat Rev Primers Methods, 2024), and (iii) the curation and quality control of public TCR databases (Jouannet et al., NAR Genomics and Bioinformatics 2025). The current study applies these optimized and peer-reviewed pipelines, along with additional internal quality controls that we have been implemented over the years, ensuring the highest possible analytical standards for TCR repertoire studies.

We therefore respectfully feel that the phrase “insufficient analytical rigor” does not accurately reflect the methodological robustness of our work. This perception is also in contrast to the comment made by one of the reviewers, who explicitly noted that “overall, the methodologies appear to be sound.”

We would therefore be grateful if, upon reviewing our detailed point-by-point responses, the editors could reconsider this statement and tone it down in the final editorial summary.

With regard to comment that our results “incompletely support the central claims”, we will leave it to the reader’s judgement. We believe that our work provides a robust and transparent basis for future research into TCR repertoire, autoimmunity, and women’s health.

Reviewer 1 (Public reviews):

Summary

The goal of this paper was to determine whether the T cell receptor (TCR) repertoire differs between a male and a female human. To address this, this group sequenced TCRs from doublepositive and single-positive thymocytes in male and female humans of various ages. Such an analysis on sorted thymocyte subsets has not been performed in the past. The only comparable dataset is a pediatric thymocyte dataset where total thymocytes were sorted.

They report on participant ages and sexes, but not on ethnicity, race, nor provide information about HLA typing of individuals. Though the experiments themselves are heroic, they do represent a relatively small sampling of diverse humans. They observed no differences in TCRbeta or TCRalpha usage, combinational diversity, or differences in the length of the CDR3 region, or amino acid usage in the CD3aa region between males or females. Though they observed some TCRbeta CD3aa sequence motifs that differed between males and females, these findings could not be replicated using an external dataset and therefore were not generalizable to the human population.

They also compared TCRbeta sequences against those identified in the past using computational approaches to recognize cancer-, bacterial-, viral-, or autoimmune-antigens. They found very little overlap of their sequences with these annotated sequences (depending on the individual, ranging from 0.82-3.58% of sequences). Within the sequences that were in overlap, they found that certain sequences against autoimmune or bacterial antigens were significantly over-represented in female versus male CD8 SP cells. Since no other comparable dataset is available, they could not conclude whether this is a finding that is generalizable to the human population.

Strengths:

This is a novel dataset. Overall, the methodologies appear to be sound. There was an attempt to replicate their findings in cases where an appropriate dataset was available. I agree that there are no gross differences in TCR diversity between males and females.

We appreciate the positive feedback from the reviewer regarding these points.

Weaknesses:

Overall, the sample size is small given that it is an outbred population. The cleaner experiment would have been to study the impact of sex in a number of inbred MHC I/II identical mouse strains or in humans with HLA-identical backgrounds.

We respectfully disagree with the reviewer’s statement. We firmly believe that the issue we are dealing with, namely sex-based differences in thymic TCR selection relevant to autoimmunity, should be investigated more thoroughly in the general human population than in inbred mouse models.

While inbred mouse strains, being MHC I/II identical, eliminate the complexity of MHC variation, this comes at the cost of biological relevance. Firstly, a discrepancy in TCR generation or selection may only become apparent under specific MHC contexts, which could easily be overlooked when studying a single inbred strain. Secondly, inbred strains frequently contain fixed genetic variants that may influence thymic selection or immune regulation. This has the potential to introduce confounding effects rather than reducing them and not solving the generalization issue.

We are in full agreement that an HLA-matched human cohort would reduce inter-individual variability. However, such sampling is impossible in practice, as our thymic tissues were obtained from deceased organ donors, a collection effort that was, as the reviewer rightly noted, “heroic”. Despite these inherent limitations, the patterns we observed were consistent across multiple analytical approaches, lending robustness to our findings.

We now explicitly acknowledge this limitation in the Discussion of the revised manuscript and explain why, despite this constraint, our study provides meaningful and biologically relevant insights into human TCR selection and sex-related immune differences.

It is unclear whether there was consensus between the three databases they used regarding the antigens recognized by the TCR sequences. Given the very low overlap between the TCR sequences identified in these databases and their dataset, and the lack of replication, they should tone down their excitement about the CD8 T cell sequences recognizing autoimmune and bacterial antigens being over-represented in females.

The three databases used in this study - McPAS-TCR, IEDB, and VDJdb - provide complementary and partially non-overlapping specificity landscapes. McPAS-TCR is enriched for pathology-associated TCRs, while IEDB and VDJdb contain a higher proportion of viral specificities. Combining them therefore broadens the antigenic spectrum accessible for analysis and represents the most comprehensive approach currently possible to capture the diversity of TCR–antigen annotations.

With regard to the limited overlap between our dataset and these databases, this observation should be interpreted with caution. While the overlap may appear minimal at first glance, it is a biologically significant phenomenon. The public databases collectively contain only a minute fraction of the total universe of TCR specificities, estimated to exceed 10^15-21 possible receptors in humans. In this context, the observation of any overlap at all, particularly with coherent biological patterns such as the overrepresentation of autoimmune- and bacterialassociated TCRs in females, is noteworthy.

We have included a short clarification in the Discussion of the revised manuscript to make this point explicit and to further temper the language describing this finding.

The dataset could be valuable to the community.

We thank the reviewer for highlighting the potential value of this dataset to the community. It will be made publicly available on the NCBI website. We would like to clarify that our intention has always been to make this dataset publicly available; therefore, we take back any incorrect suggestions made in the original submission.

Reviewer #1 (Recommendations for the authors):

I would just recommend toning down the excitement about autoimmune TCRs being overrepresented in females. Then the conclusions will be in alignment with their results.

We thank the reviewer for this constructive recommendation. We would like to express our full support for the editorial transparency policies of eLife, which allow readers to access to both the reviewers’ comments and our detailed responses, enabling them to form their own informed opinions regarding our conclusions.

Nevertheless, we have moderated some of our wording.

Reviewer #2 (Public review):

Summary:

This study addresses the hypothesis that the strikingly higher prevalence of autoimmune diseases in women could be the result of biased thymic generation or selection of TCR repertoires. The biological question is important, and the hypothesis is valuable. Although the topic is conceptually interesting and the dataset is rich, the study has a number of major issues that require substantial improvement. In several instances, the authors conclude that there are no sex-associated differences for specific parameters, yet inspection of the data suggests visible trends that are not properly quantified. The authors should either apply more appropriate statistical approaches to test these trends or provide stronger evidence that the observed differences are not significant. In other analyses, the authors report the differences between sexes based on a pulled analysis of TCR sequences from all the donors, which could result in differences driven by one or two single donors (e.g., having particular HLA variants) rather than reflect sex-related differences.

Strengths:

The key strength of this work is the newly generated dataset of TCR repertoires from sorted thymocyte subsets (DP and SP populations). This approach enables the authors to distinguish between biases in TCR generation (DP) and thymic selection (SP). Bulk TCR sequencing allows deeper repertoire coverage than single-cell approaches, which is valuable here, although the absence of TRA-TRB pairing and HLA context limits the interpretability of antigen specificity analyses. Importantly, this dataset represents a valuable community resource and should be openly deposited rather than being "available upon request."

We thank the reviewer for highlighting the potential value of this dataset to the community. It will be made publicly available on the NCBI website. We would like to clarify that our intention has always been to make this dataset publicly available; therefore, we take back any incorrect suggestions made in the original submission.

Weaknesses:

Major:

The authors state that there is "no clear separation in PCA for both TRA and TRB across all subsets." However, Figure 2 shows a visible separation for DP thymocytes (especially TRA, and to a lesser degree TRB) and also for TRA of Tregs. This apparent structure should be acknowledged and discussed rather than dismissed.

We thank the reviewer for this careful observation. Discussing apparent “trends” rather than statistically significant results is indeed a nuanced issue, as over-interpretation of visual patterns is usually discouraged. We agree that, within the specific context of TCR repertoire analyses, visual structures in multivariate projections such as PCA can provide useful contextual information.

However, we have not identified a striking trend in our representation. We therefore chose to avoid overemphasizing these visual impressions in the text.

Supplementary Figures 2-5 involve many comparisons, yet no correction for multiple testing appears to be applied. After appropriate correction, all the reported differences would likely lose significance. These analyses must be re-evaluated with proper multiple-testing correction, and apparent differences should be tested for reproducibility in an external dataset (for example, the pediatric thymus and peripheral blood repertoires later used for motif validation).

As is standard in exploratory immunogenomic studies, including TCR repertoire analyses, our objective was to uncover broad biological patterns rather than to establish definitive statistical associations. In analyses that are discovery-oriented, correction for multiple testing, while essential in confirmatory contexts, is not mandatory and may even obscure meaningful trends by inflating type II error rates. Our objective was therefore to highlight consistent directional patterns across analytical layers, to guide future confirmatory work rather than to make categorical claims.

We also note that this comment somewhat contrasts with the earlier suggestion to discuss trends that are not statistically significant.

With regard to the proposal to verify our observations using an external dataset, we are in full agreement that independent confirmation would be beneficial. However, as reviewer 1 rightly emphasized, the generation of such datasets from sorted human thymocyte subsets is “heroic” and has rarely, if ever, been achieved. We are aware of no existing dataset that provides comparable material or analytical depth.

The available single-cell thymic dataset (Park et al., Science 2020) includes only a few hundred sequences per donor, which is significantly less than the number of sequences in our study. This limited dataset is not adequate for cross-validation or for representing the full complexity of thymic TCR repertoires.

As with the pediatric thymus dataset, the lack of statistical power in the dataset due to the small number of female subjects (only three) means that sex-related differences in V/J usage cannot be evaluated.

Finally, the peripheral blood dataset is not appropriate for validating thymic generation or selection processes, as it reflects post-thymic selection and antigen-driven remodeling, making it impossible to distinguish peripheral effects from thymic influences.

For these reasons, none of the currently available datasets provides a sufficiently clean or powerful framework to test the reproducibility of subtle sex-associated effects on thymic TCR repertoires. Nevertheless, we fully agree that confirmation in an independent and larger cohort will be an important next step to refine these exploratory findings and assess their generalizability to a broader human population.

Supplementary Figure 6 suggests that women consistently show higher Rényi entropies across all subsets. Although individual p-values are borderline, the consistent direction of change is notable. The authors should apply an integrated statistical test across subsets (for example, a mixed-effects model) to determine whether there is an overall significant trend toward higher diversity in females.

We agree that Rényi entropies tend to show a consistent direction of change across subsets, with slightly higher values observed in females. In this section, our objective was to provide a descriptive overview of diversity patterns for each thymic subset. This is because these subsets are biologically distinct and therefore require individual analysis, as we previously demonstrated using the same dataset (Isacchini et al, PRX Life. 2024). Therefore, while a mixed-effects approach could in principle be applied to test for an overall trend, such an analysis would rely on the assumption of a common sex effect across heterogeneous cell types.

It is important to note that the complete dataset has now been made publicly available, enabling interested researchers to perform additional integrative or model-based analyses to further explore these diversity trends.

Figures 4B and S8 clearly indicate enrichment of hydrophobic residues in female CDR3s for both TRA and TRB (excluding alanine, which is not strongly hydrophobic). Because CDR3 hydrophobicity has been linked to increased cross-reactivity and self-reactivity (see, e.g., Stadinski et al., Nat Immunol 2016), this observation is biologically meaningful and consistent with higher autoimmune susceptibility in females.

We thank the reviewer for this insightful comment.

As correctly noted, increased hydrophobicity at specific CDR3β positions has been linked to enhanced cross-reactivity and self-reactivity, as described by Stadinski et al. (Nat Immunol 2016), and we reference this work in the manuscript.

In our analysis corresponding to Figure 4B (TRB), hydrophobicity was quantified at the sequence level by computing, for each unique CDR3β sequence, the overall proportion of hydrophobic amino acids across the CDR3 loop. This approach aligns with that of Lagattuta et al. (Nat Immunol 2022), whose code we adapted to accommodate longer CDR3s. This global hydrophobicity metric captures overall composition, but, by its construction, does not account for positional context, the key mechanism implicated by Stadinski et al.

As outlined in our original Figure 4C, the results were obtained through a position-based amino acid analysis. For each CDR3β sequence, we extracted the amino acid at every IMGTdefined CDR3 position (p104–p118) and quantified, at each position, the percentage of unique sequences containing each amino acid. Positions p109 and p110 correspond to the p6–p7 sites highlighted by Stadinski et al. as functionally relevant for self-reactivity. This analysis evaluates positional composition independently of clonotype frequency, focusing specifically on hydrophobic amino acid classes.

Following the recommendation of the reviewer, the revised manuscript has removed alanine (which is only weakly hydrophobic) has been excluded from the hydrophobic residue set. With this refined definition, we observe a significant enrichment of hydrophobic amino acids at p109 in CD8 T cell repertoires from females, with similar but non-significant trends at p109 in DP and CD4 Teff cells and at p110 in CD8 cells (see new Figure 4C).

As outlined in the revised Methods, Results, and Discussion sections, Figure 4C focuses exclusively on positional hydrophobic amino acid usage. This was previously implicit, although it was noted in the legend and visually represented in the plots.

The majority of "hundreds of sex-specific motifs" are probably donor-specific motifs confounded by HLA restriction. This interpretation is supported by the failure to validate motifs in external datasets (pediatric thymus, peripheral blood). The authors should restrict analysis to public motifs (shared across multiple donors) and report the number of donors contributing to each motif.

We fully agree that donor-specific and HLA-restricted motifs represent a major potential confounder in repertoire-level comparisons. To minimize this potential bias, our analysis was explicitly restricted to public motifs, as clearly stated in the Materials and Methods section:

“Additional filters were applied so that: (i) a motif includes public CDR3aa sequences (shared by at least two individuals); (ii) a significant enrichment is detected (Fisher’s exact test, p < 0.01); and (iii) a usage difference between groups of at least twofold (Wilcoxon test, p < 0.05).”

Accordingly, every motif reported in the manuscript is supported by at least two independent donors, ensuring that no motif reflects an individual- or HLA-specific effect (see Supplementary Figures 10-13[previously Supplementary Figure 9]). We have now added a more explicit mention of the number of donors contributing to each motif in the figure legend and have clarified this point in the revised Methods and Results sections to make this criterion more visible to readers.

When comparing TCRs to VDJdb or other databases, it is critical to consider HLA restriction. Only database matches corresponding to epitopes that can be presented by the donor's HLA should be counted. The authors must either perform HLA typing or explicitly discuss this limitation and how it affects their conclusions.

We respectfully disagree with the assertion that HLA typing is necessary for the type of comparative analysis we have conducted. While it is true that HLA molecules present peptides to TCRs and thereby contribute to the tripartite interaction determining T cell activation, extensive evidence indicates that the CDR3 region, particularly CDR3β, is the dominant determinant of antigen specificity. This finding is supported by structural and computational studies (Madi et al., eLife, 2017; Huang et al., Nat. Biotech., 2020; MayerBlackwell et al., Methods Mol. Biol., 2022) showing that CDR3β residues are responsible for the majority of peptide contacts, whereas CDR1 and CDR2 primarily interact with the MHC framework.

As emphasized in several recent benchmarking studies (e.g., Springer et al., Front Immunol, 2021), CDR3β sequence composition alone captures most of the information required for specificity inference. Consequently, widely used and validated computational tools such as GIANA (Zhang et al. Nat. Commun. 2021), iSMART (Zhang et al. Clin. Cancer Res. 2020), and ATMTCR (Cai et al. Front. Immunol. 2022) rely exclusively on CDR3β aminoacid sequences and still achieve high predictive performance.

Our analysis aligns with this well-established paradigm. While we agree that integrating donor HLA typing would refine epitope-level annotation and reduce potential noise, the absence of HLA data does not invalidate the comparative framework we used, which focuses on relative representation of annotated specificities across groups rather than on individual TCR–HLA–peptide triads.

Although the age distributions of male and female donors are similar, the key question is whether HLA alleles are similarly distributed. If women in the cohort happen to carry autoimmuneassociated alleles more often, this alone could explain observed repertoire differences. HLA typing and HLA comparison between sexes are therefore essential.

To address the issue of any potential differences in HLA background, we examined the subset of adult donors for whom HLA typing information was available (HLA-A, HLA-B, HLADR, and HLA-DQB; n = 16). Within this subset, the distribution of HLA alleles was relatively balanced between males and females (as illustrated by the heatmap showing HLA class II expression patterns and HLA class I family grouping in Author response image 1). This analysis suggests that the sex-associated differences in the repertoire observed in our study are unlikely to be driven solely by unequal representation of autoimmune-associated HLA alleles.

We acknowledge, however, that complete HLA information was not available for all donors, which remains a limitation of the dataset.

Author response image 1.

In some analyses (e.g., Figures 8C-D) data are shown per donor, while others (e.g., Fig. 8A-B) pool all sequences. This inconsistency is concerning. The apparent enrichment of autoimmune or bacterial specificities in females could be driven by one or two donors with particular HLAs. All analyses should display donor-level values, not pooled data.

While Figures 8A–B present pooled data to summarize global trends, the corresponding donor-level analyses were provided in Supplementary Figures 15B and 16 (previously Supplementary Figures 11B and 12). In these, each individual is shown separately, with each point representing an individual. It is important to note that these donor-resolved plots do not reveal any sample-specific driver: the patterns observed in the pooled data remain consistent across donors, without any single individual accounting for the apparent enrichments. As outlined in the revised manuscript, readers now directed to the relevant supplementary figures for further clarification.

The reported enrichment of matches to certain specificities relative to the database composition is conceptually problematic. Because the reference database has an arbitrary distribution of epitopes, enrichment relative to it lacks biological meaning. HLA distribution in the studied patients and HLA restrictions of antigens in the database could be completely different, which could alone explain enrichment and depletions for particular specificities. Moreover, differences in Pgen distributions across epitopes can produce apparent enrichment artifacts. Exact matches typically correspond to high-Pgen "public" sequences; thus, the enrichment analysis may simply reflect variation in Pgen of specific TCRs (i.e., fraction of high-Pgen TCRs) across epitopes rather than true selection. Consequently, statements such as "We observed a significant enrichment of unique TRB CDR3aa sequences specific to self-antigens" should be removed.

We respectfully disagree with the conclusion that our enrichment analysis lacks biological meaning. Our approach directly involves a direct comparison of the same set of observed TCR sequences between males and females. Consequently, any potential biases related to generation probability (Pgen), which affect all sequences equally, cannot account for the observed sex-specific differences. To summarize, because the comparison is performed on the same set of sequences, changes in the probability of generation across epitopes cannot explain the differences seen between the sexes.

We do agree, however, that the composition of the reference databases may influence apparent enrichment patterns, as these resources contain uneven distributions of epitope categories and often incomplete information regarding HLA restriction. It should be noted that this limitation is inherent to all database-based annotation approaches, a fact which is explicitly acknowledged in the revised Discussion.

The overrepresentation of self-specific TCRs in females is the manuscript's most interesting finding, yet it is not described in detail. The authors should list the corresponding self-antigens, indicate which autoimmune diseases they relate to, and show per-donor distributions of these matches.

We thank the reviewer for this constructive suggestion.

As recommended, we have expanded the description of the self-specific TCRs identified in our dataset and now provide this information in Supplementary Table 2 of the revised manuscript. Specifically, the table lists the corresponding self-antigens and the autoimmune diseases with which they are associated. In our curated database, these annotations primarily correspond to celiac disease and type 1 diabetes, which were the two autoimmune contexts explicitly defined in the manually curated reference datasets.

For the “cancer” specificity group, we have clarified that antigen assignments were established based on (i) annotations available in the original databases (IEDB, VDJdb, McPAS-TCR) and (ii) cross-referencing with additional resources, including the Human Protein Atlas, the Cancer Antigenic Peptide Database (de Duve Institute), and the Cancer Antigen Atlas (Yi et al., iScience 2021), to ensure consistency in the classification of cancer and neoantigen specificities. Please refer to the Materials and Methods section for a full description of the procedure for this specific assignment.

Donor-level distributions of these self-specific matches are now shown in Supplementary Figures 15B and 16 (previously Supplemental Figures 11B and 12), allowing direct visualization of inter-donor variability. Importantly, these plots confirm that the observed enrichment in females is not driven by a single individual, further supporting the robustness of the finding.

The concept of poly-specificity is controversial. The authors should clearly explain how polyspecific TCRs were defined in this study and highlight that the experimental evidence supporting true polyspecificity is very limited (e.g., just a single TCR from Figure 5 from Quiniou et al.).

We certainly agree (and regret) that the concept of TCR polyspecificity remains a subject of debate and often underappreciated in the field of immunology. As Don Mason famously discussed in his seminal essay “A very high cross-reactivity is an essential feature of the TCR” (doi: 10.1016/S0167-5699(98)01299-7) published over 25 years ago, both theoretical and experimental evidence indicates that each TCR can, in principle, recognize millions of distinct peptides, albeit with variable avidity.

Although this principle is widely accepted, it is frequently overlooked in the field of experimental immunology. In this area, anything that deviates from strict monospecificity is often disregarded as noise.

In our own analyses of large-scale TCR repertoires, we have repeatedly observed that many CDR3 sequences are annotated with multiple specificities across different databases, often corresponding to peptides from unrelated organisms. As demonstrated in Quiniou et al. (eLife 2023), such polyreactive TCRs exhibit distinctive features, including biased physicochemical composition, and tend to be enriched in various biological contexts. In our preliminary study of such TCRs, which have the capacity to be specific for multiple viral- and self- epitopes, we hypothesized that they may serve as a first line of defense against pathogens and also be involved in triggering autoimmunity. We therefore consider it important to report this phenomenon rather than omit it, especially given its potential relevance to both protective immunity and autoimmunity.

In the present study, polyspecific TCRs were defined operationally as TRB CDR3aa sequences associated with a minimum of two distinct specificity groups, corresponding either to different microbial species or to multiple antigen categories within the curated database. Therefore, our definition captures broader antigenic groupings rather than epitope-level binding events.

We fully acknowledge that direct experimental evidence for true molecular-level polyspecificity remains limited. Indeed, as the reviewer notes, only a single TCR with multiepitope reactivity has been rigorously demonstrated to date (Quiniou et al.2023). Consequently, our analysis does not make claims about structural promiscuity; instead, it uses database-annotated cross-reactivity as a proxy to explore broader repertoire-level patterns.

As outlined in the Methods section, this definition has been clarified and its discussion expanded in the Discussion to explicitly address these conceptual and methodological nuances.

Minor:

Clarify why the Pgen model was used only for DP and CD8 subsets and not for others.

As noted, computing Pgen values involves two steps: (i) training a generative model of V(D)J recombination using IGoR, and (ii) estimating generation probabilities with OLGA based on that model. Both steps require a significant amount of computing power, especially when applied to large repertoires across multiple subsets. For this reason, we focused the analysis on DP thymocytes, which represent the repertoire prior to thymic selection, and CD8 T cells after CD8 selection.

The Methods section should define what a "high sequence reliability score" is and describe precisely how the "harmonized" database was constructed.

Briefly, the annotated database used in this study was constructed in accordance with the procedure established in our previously published work (Jouannet et al., NAR Genomics and Bioinformatics, 2025). The study integrates three publicly available resources, IEDB, VDJdb, and McPAS-TCR, which were collected as of October 2023. These three datasets were then merged into a single harmonized compendium, undergoing extensive standardization. When entries shared identical information across databases (same V–CDR3–J for both TRA and TRB, same epitope, organism, PubMed ID, and cell subset), only one representative was kept; discrepant or incomplete entries were retained to preserve information. We then assigned a sequence reliability score, the Verified Score (VS), following the verification strategy used by IEDB. The scale ranges from 0 to 2 and reflects the concordance between calculated and curated TRA/TRB CDR3 sequences (2 = both TRA and TRB present are verified, 1.1 = only TRA verified, 1.2 = only TRB verified, 0 = no verified chain). A second score, the Antigen Identification Score (AIS), is used to rank antigen-identification methods on a scale of 0 to 5, according to the strength of the experimental evidence supporting them.

In the present study, “high reliability” refers to sequences with a verified TRB CDR3aa chain (VS ≥ 1.2) and an AIS score corresponding to T cells in vitro stimulation with a pathogen, protein or peptide, or pMHC X-mer sorting (> 3.2, excluding categories 4.1 and 4.2), ensuring that downstream analyses were performed on a rigorously curated and biologically trustworthy dataset. The Methods section now explicitly details these criteria.

The statement "we generated 20,000 permuted mixed-sex groups" is unclear. It is not evident how this permutation corrects for individual variation or sex bias. A more appropriate approach would be to train the Pgen model separately for each individual's nonproductive sequences (if the number of sequences is large enough).

The objective of this analysis was to determine whether the enrichment of TRBV06-5 in females was due to random grouping of individuals or whether it was attributable to sex itself. To do so, we generated all possible perfectly mixed groups of donors (i.e., groups containing an equal number of male and female donors) for the concerned thymocyte subset, and then performed 20,000 random pairwise comparisons between such mixed groups. For each comparison, we tested the TRBV06-5 usage between the two mixed groups. This procedure directly evaluates whether group composition (independent of sex) could spuriously generate differences in TRBV usage. Notably, none of these 20,000 comparisons between the two mixed groups yielded a statistically significant difference in TRBV06-5 usage. In contrast, when comparing the true male and female groups, a significant difference was identified. This demonstrates that the signal we observe is not driven by random donor grouping or individual-level variation, but is specifically associated with sex. It is important to note that this analysis, which is designed to exclude spurious group effects, is rarely performed in published repertoire studies, yet it provides an important internal control for robustness.

Reviewer #2 (Recommendations for the authors):

(1) Data availability "upon request" is unacceptable. All raw and processed data, as well as scripts used for analysis and figure generation, must be publicly deposited before publication.

We would like to clarify that our intention has always been to make this dataset publicly available. It was a mistake to suggest otherwise in the original submission.

(2) At the beginning of the Results section, include a brief description of the dataset: number of donors, sex ratio, age range, number of samples per subset, and sorting strategy. Although Figure 1 shows this, the information should also be mentioned in the main text.

In line with the recommendation, we have now added a summary of the cohort characteristics at the beginning of the Results section. This includes the number of donors, sex ratio, age range, number of samples per subset, and the sorting strategy used. While this information was already included in Figure 1, we concur that including it directly in the main text enhances readability.

(3) Report the number of cells and unique clonotypes analyzed per individual. Rank-frequency plots (in log-log coordinates) would be helpful.

We have now added, for each donor and each subset, the number of cells, and additionally for each chain, the number of total and unique clonotypes analyzed. This information is provided in the revised manuscript in a new supplementary table (Supplemental Table 1).

These plots have been integrated into the revised manuscript as Supplementary Figure 2.

(4) For analysis in Figure 4B, the total fraction of hydrophobic amino acids should be calculated for each patient separately, and values for men and women should be compared (analogously to Figure 4C, but for the whole CDR3 and excluding alanine).

Please note that the TRB CDR3aa composition in Figure 4B has already been quantified at the individual level. For each unique TRB CDR3aa sequence, we computed the proportion of each of the 20 amino acids across the CDR3β loop, then summarized these values per donor (mean per individual). The log2 fold change displayed in Figure 4B (and supplemental Figure 9 for TRA) is calculated from the median donor-level values for females versus males, rather than from pooled CDR3s. It is intended as descriptive, “global” view of amino acid usage within the central CDR3 region. Hydrophobicity was not used directly in the computation, but is indicated only by bar color, based on the Kyte-Doolittle- derived IMGT classification. This provides an observational overview of amino acid composition in the central CDR3 region.

As the mechanistic link between hydrophobicity and self-reactivity described by Stadinski et al. is explicitly position-dependent, we consider positional analyses to be the most appropriate method for formally interrogating this hypothesis, as we did in Figure 4C. Here, our primary focus was on the position-specific usage of hydrophobic amino acids at IMGT positions p109-p110. These positions correspond to the central p6-p7 positions described by Stadinski et al. For each individual, we computed the proportion of unique TRB CDR3aa sequences carrying a hydrophobic amino acid at a given position.

Accordingly, in the revised manuscript we refined the Figure 4C by excluding alanine due to its weak hydrophobic property (as recommended by the reviewer) This positional composition analysis now reveals a statistically significant increase in hydrophobic usage at p109 in female CD8 repertoires, with similar, though non-significant, trends at p109 in DP and CD4Teff ad at p110 in CD8 cells. Figure 4B is therefore retained as an exploratory overview of amino acid composition usage along the CDR3 loop, while Figure 4C is used for the more specific question of hydrophobicity and potential cross-reactivity.

The Methods section has been expanded to provide clearer descriptions of these computations, and the Results and Discussion sections corresponding to Figures 4B-C (and supplemental Figure 9) have been revised to make the rationale, implementation, and interpretation of these hydrophobicity analyses more explicit.

(5) Figure 6 shows a trend toward higher clustering of Treg TCRs in males, which could relate to the lower incidence of autoimmunity in men. The authors could test whether specific Treg clusters are male-specific and shared among male donors.

As shown in Figure 6, a clear trend towards higher similarity among Treg CDR3aa sequences in males is evident, as indicated by the proportion of sequences included in clusters and in the overall similarity density. However, identifying “male-specific clusters” shared across donors is not straightforward in our analytical framework.

In our approach, for each cell subset, CDR3aa sequences were downsampled 100 times to the smallest sample size, and clustering was repeated at each iteration. Therefore, the clusters’ identities are not consistent across iterations. The clusters depend on the specific subset of sequences selected at each downsampling step, as well as on their underlying Pgen distribution. Therefore, it is not possible to reliably assess whether specific clusters are systematically “male-shared”. This is because cluster composition is a function of stochastic resampling rather than of biological structure. For this reason, a comparison of cluster identities across donors would not produce interpretable results.

Synthèse : Décryptage des Labels et Accréditations de l'Enseignement Supérieur sur Parcoursup

Ce document de briefing synthétise les interventions d'Ariane Ferreri et de Thibaut Cojean (L'Étudiant) lors du webinaire organisé en partenariat avec la FCPE.

Il vise à fournir une grille de lecture précise des labels, diplômes et certifications rencontrés sur la plateforme Parcoursup pour aider les familles à évaluer la qualité réelle des formations.

Résumé Exécutif

Face à une offre de formation de plus en plus vaste, la distinction entre reconnaissance académique officielle et promesses marketing est cruciale. Les points clés à retenir sont :

• La primauté du Grade et du Visa : Seuls les diplômes bénéficiant d'un « grade » (Licence ou Master) ou d'un « visa » de l'État garantissent une équivalence académique permettant la poursuite d'études.

• Le piège du RNCP : Un titre RNCP atteste d'une qualification professionnelle mais ne possède aucune valeur académique intrinsèque (pas de crédits ECTS automatiques, pas de garantie de poursuite d'études en master).

• La vigilance sur le privé lucratif : Un projet de loi est en cours pour mieux réguler ce secteur, mais en attendant, l'examen des labels (EESPIG, CTI) et des audits (hexagone bleu sur Parcoursup) reste la meilleure protection.

• L'importance des crédits ECTS : Ils sont l'unité de mesure européenne (60 par an) indispensable pour la mobilité et la validation des acquis.

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1. Les Fondamentaux de la Reconnaissance Académique

Le système des crédits ECTS

Les crédits ECTS (European Credit Transfer System) constituent une unité de mesure européenne de la formation.

• Volume : Une année d'enseignement supérieur correspond à 60 crédits.

• Utilité : Ils garantissent la reconnaissance du parcours auprès d'autres établissements, en France comme en Europe.

Sans ECTS, une poursuite d'études (ex: passer d'une Licence à un Master) est compromise.

• Validation : Les crédits sont affiliés à des modules spécifiques (matières, projets associatifs, etc.).

Si un module échoue, seuls les crédits associés manquent à l'étudiant.

Diplômes Nationaux vs Écoles Privées

| Type de Diplôme | Caractéristiques | Exemples | | --- | --- | --- | | Diplôme National | Organisé par l'État, délivré au nom d'un ministère. | BTS, Licence, Master, Doctorat, BUT, DNA (Art). | | Diplôme Visé | Diplôme d'une école privée reconnu par l'État pour sa qualité. | Bachelors de certaines écoles de commerce. | | Grade de Licence/Master | Niveau de reconnaissance maximal pour un diplôme non national. | Diplômes d'Ingénieurs, certains bachelors d'excellence. |

Note importante : Une école peut être reconnue par l'État mais proposer des formations qui ne le sont pas. Il faut impérativement vérifier la reconnaissance de la formation précise visée.

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2. Analyse Détaillée des Labels et Accréditations

Les labels d'excellence et d'intérêt général

• EESPIG (Établissement d'Enseignement Supérieur Privé d'Intérêt Général) : Label attribué à des établissements privés à but non lucratif qui remplissent une mission de service public.

Il concerne environ 60 grandes écoles en France.

• CTI (Commission des Titres d'Ingénieur) : Organisme unique habilité à autoriser les écoles à délivrer le titre d'ingénieur.

Une « formation en ingénierie » n'est pas une « formation d'ingénieur » si elle n'est pas accréditée par la CTI.

• DD&RS (Développement Durable et Responsabilité Sociétale) : Label difficile à obtenir attestant d'un engagement écologique et social.

C'est un gage de sérieux académique et de structuration de la communauté enseignante.

Les accréditations internationales (Écoles de Commerce)

Pour les écoles de management, la « Triple Couronne » désigne la possession des trois accréditations suivantes :

• AACSB (Américain)

• EQUIS (Européen)

• AMBA (Britannique)

La France possède la plus forte proportion au monde d'écoles titulaires de cette triple accréditation, ce qui garantit un audit rigoureux des processus pédagogiques.

Les certifications professionnelles (Vigilance requise)

• RNCP (Répertoire National des Certifications Professionnelles) : Ce label atteste que la formation prépare à un métier reconnu par le marché du travail.

Attention : il n'a aucune valeur académique.

Une formation RNCP seule ne permet pas de poursuivre des études à l'université ou en master sans passer par une procédure complexe de validation des acquis (VAE/VAPP).

• Qualiopi : C'est un label de processus qualité obligatoire pour les organismes recevant des fonds publics (notamment pour l'apprentissage).

Il ne préjuge en rien de la qualité pédagogique ou de la valeur académique du diplôme.

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3. Guide de Vigilance sur Parcoursup

Les indicateurs de fiabilité

• L'Hexagone Bleu : Sur Parcoursup, la présence d'un logo hexagonal bleu indique que la formation est contrôlée par l'État.

• Le drapeau bleu-blanc-rouge : Méfiance.

N'importe quelle école peut l'utiliser sur une brochure commerciale sans que cela ne repose sur une règle officielle.

• Le statut "Sous Contrat" : Pour les lycées privés (BTS, CPGE), ce statut garantit que les enseignants sont payés par l'État et appliquent le programme national.

Les signaux d'alerte ("Red Flags")

• Argumentaire centré exclusivement sur le RNCP : Signifie souvent l'absence de reconnaissance académique.

• Formations 100% à distance en post-bac : Très risqué pour des jeunes sortant du lycée nécessitant un encadrement pour réussir la transition vers le supérieur.

• Absence de corps professoral permanent : Une école n'utilisant que des intervenants extérieurs (professionnels) manque souvent de structure pédagogique.

• Modèle économique basé uniquement sur l'alternance : Peut poser des questions sur la pérennité et l'investissement académique réel de l'établissement.

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4. Recommandations Méthodologiques pour les Familles

Pour valider la qualité d'une formation, il est conseillé de multiplier les sources d'information :

• Vérification des listes officielles : Consulter les sites de la CTI (ingénieurs), de la CGE (Conférence des Grandes Écoles) ou le portail du Ministère du Travail pour le RNCP.

• Utilisation de LinkedIn : Contacter d'anciens étudiants pour connaître leur parcours réel et solliciter des entreprises du secteur pour savoir si elles reconnaissent et recrutent les diplômés de l'école visée.

• Questionnement direct en JPO (Journées Portes Ouvertes) :

  • « Jusqu'à quand votre visa ou grade est-il valable ? » (un renouvellement court de 3 ans peut signaler des difficultés, contre 5 ans pour l'excellence).

• « Quel est le réseau d'anciens et puis-je avoir des contacts ? »

• « Où vont vos étudiants après le Bachelor ? » (Si la réponse est floue, la poursuite d'études est probablement difficile).

Perspective législative

Le gouvernement prépare une loi pour le printemps afin de mieux réguler l'enseignement privé lucratif.

Ce projet prévoit de catégoriser les formations sur Parcoursup entre celles bénéficiant d'une certification automatique de qualité (grades, EESPIG) et celles soumises à des audits renforcés.

Author response:

The following is the authors’ response to the original reviews

We thank the reviewers for their constructive feedback, which has helped preparing a substantially improved manuscript. In response to concerns about the conceptual distinction between prediction and stimulus dependency, we have fundamentally restructured the paper around the notion of passive control systems. This involved rewriting the Abstract, Introduction, and large portions of the Results (~60% of text revised).

Key changes:

- New analyses on Goldstein et al. (2022) data. We demonstrate that our findings—including the insufficiency of proposed corrections—generalise to the original dataset (Figures S2B, S3B, S5C, S6B).

- Clarified novel contribution. We now make explicit that prior control analyses (residualisation, bigram removal) do not address the concern, because hallmarks persist in passive systems that cannot predict.

- Proposed criterion for future work. Pre-onset neural encoding can only count as evidence for prediction if it exceeds a passive baseline (e.g., acoustics).

We believe the revision offers a clearer, more rigorous contribution and provides a constructive framework for evaluating claims of neural prediction.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper tackles an important question: What drives the predictability of pre-stimulus brain activity? The authors challenge the claim that "pre-onset" encoding effects in naturalistic language data have to reflect the brain predicting the upcoming word. They lay out an alternative explanation: because language has statistical structure and dependencies, the "pre-onset" effect might arise from these dependencies, instead of active prediction. The authors analyze two MEG datasets with naturalistic data.

Strengths:

The paper proposes a very reasonable alternative hypothesis for claims in prior work. Two independent datasets are analyzed. The analyses with the most and least predictive words are clever, and nicely complement the more naturalistic analyses.

Weaknesses:

I have to admit that I have a hard time understanding one conceptual aspect of the work, and a few technical aspects of the analyses are unclear to me. Conceptually, I am not clear on why stimulus dependencies need to be different from those of prediction. Yes, it is true that actively predicting an upcoming word is different from just letting the regression model pick up on stimulus dependencies, but given that humans are statistical learners, we also just pick up on stimulus dependencies, and is that different from prediction? Isn't that in some way, the definition of prediction (sensitivity to stimulus dependencies, and anticipating the most likely upcoming input(s))?

We thank the reviewer for this comment, which highlights that the previous version wasn’t sufficiently clear. Conceptually, the difference is critical: it is the difference between passively encoding or representing the stimulus (like e.g., a spectrogram of the stimulus would), and actively generating predictions.

We have substantially changed the framing of the paper to put the notion of control systems centre-stage. One such control system is the speech acoustics: they encode the stimulus (and thus its dependencies) but cannot predict. When we observe the "hallmarks of prediction" in acoustics, this demonstrates the hallmarks can arise without any prediction.

This brings me to some of the technical points: If the encoding regression model is learning one set of regression weights, how can those reflect stimulus dependencies (or am I misunderstanding which weights are learned)? Would it help to fit regression models on for instance, every second word or something (that should get rid of stimulus dependencies, but still allow to test whether the model predicts brain activity associated with words)? Or does that miss the point? I am a bit unclear as to what the actual "problem" with the encoding model analyses is, and how the stimulus dependency bias would be evident. It would be very helpful if the authors could spell out, more explicitly, the precise predictions of how the bias would be present in the encoding model.

Different weights are estimated per time point in the time-resolved regression. This allows the model to learn how the response to words unfolds, but also to learn different stimulus dependencies at each timepoint. Fitting on every second word would reduce but not eliminate the problem. Our control system approach provides a more principled test. We have clarified the mechanism in the Introduction (lines 82-90), explaining how correlations between neighbouring words allow the regression model to predict prior neural activity without assuming pre-activation.

Reviewer #2 (Public Review):

Summary:

At a high level, the reviewers demonstrate that there is an explanation for pre-word-onset predictivity in neural responses that does not invoke a theory of predictive coding or processing. The paper does this by demonstrating that this predictivity can be explained solely as a property of the local mutual information statistics of natural language. That is, the reason that pre-word onset predictivity exists could simply boil down to the common prevalence of redundant bigram or skip-gram information in natural language.

Strengths:

The paper addresses a problem of significance and uses methods from modern NeuroAI encoding model literature to do so. The arguments, both around stimulus dependencies and the problems of residualization, are compellingly motivated and point out major holes in the reasoning behind several influential papers in the field, most notably Goldstein et al. This result, together with other papers that have pointed out other serious problems in this body of work, should provoke a reconsideration of papers from encoding model literature that have promoted predictive coding. The paper also brings to the forefront issues in extremely common methods like residualization that are good to raise for those who might be tempted to use or interpret these methods incorrectly.

Weaknesses:

The authors don't completely settle the problem of whether pre-word onset predictivity is entirely explainable by stimulus dependencies, instead opting to show why naive attempts at resolving this problem (like residualization) don't work. The paper could certainly be better if the authors had managed to fully punch a hole in this.

We thank the reviewer for their assessment.

We believe our paper does punch the hole that can be punched, which is a hole in the method. Our control demonstrates that adjusting the features (X matrix) cannot address dependencies that persist in the signal itself (Y matrix). Because the hallmarks emerge in a system that cannot predict (even after linearly removing the previous stimulus) attributing pre-onset encoding performance to neural prediction (rather than stimulus structure) is fundamentally ambiguous, and different (e.g. variance partitioning) approaches would suffer from the same ambiguity. We have reframed the manuscript to make this argument more clearly.

Reviewer #3 (Public Review):

Summary:

The study by Schönmann et al. presents compelling analyses based on two MEG datasets, offering strong evidence that the pre-onset response observed in a highly influential study (Goldstein et al., 2022) can be attributed to stimulus dependencies, specifically, the auto-correlation in the stimuli—rather than to predictive processing in the brain. Given that both the pre-onset response and the encoding model are central to the landmark study, and that similar approaches have been adopted in several influential works, this manuscript is likely to be of high interest to the field. Overall, this study encourages more cautious interpretation of pre-onset responses in neural data, and the paper is well written and clearly structured.

Strengths:

(1) The authors provide clear and convincing evidence that inherent dependencies in word embeddings can lead to pre-activation of upcoming words, previously interpreted as neural predictive processing in many influential studies.

(2) They demonstrate that dependencies across representational domains (word embeddings and acoustic features) can explain the pre-onset response, and that these effects are not eliminated by regressing out neighboring word embeddings - an approach used in prior work.

(3) The study is based on two large MEG datasets, showing that results previously observed in ECoG data can be replicated in MEG. Moreover, the stimulus dependencies appear to be consistent across the two datasets.

We’d like to thank the reviewer for their comments on our preprint.

Weaknesses:

(1) To allow a more direct comparison with Goldstein et al., the authors could consider using their publicly available dataset.

We thank the reviewer for this suggestion. The Goldstein dataset was not publicly available when we conducted this research. However, we have now applied our control analyses to their stimulus material, and found that the exact same problem applies to their dataset, too.

We have added analyses of the Goldstein et al. (2022) podcast stimulus throughout the paper. Results are shown in Figures S2B, S3B, S5C, and S6B. Critically, we observe the same pattern: both hallmarks emerge in the acoustic control system, and residualisation fails to eliminate them. This demonstrates that our findings generalise to the very dataset used to establish pre-onset encoding as evidence for neural prediction.

(2) Goldstein et al. already addressed embedding dependencies and showed that their main results hold after regressing out the embedding dependencies. This may lessen the impact of the concerns about self-dependency raised here.

We thank the reviewer for raising this point, as it reveals we failed to convey a central argument in the previous version. Goldstein et al.'s control analysis did not address the concern. We show that even after the control analyses that Goldstein et al. perform (removing bigrams, regressing out embedding dependencies) the "hallmarks of prediction" still emerge when applying the analysis to a passive control system that by definition does not predict: the speech acoustics. We now also show this in their data.

To better convey this critical point, around the concept of "passive control systems". We now first establish that the hallmarks appear in acoustics (Figure 3), then show that residualisation fails to remove them (Figure 4). This makes explicit that any claim about "controlling for dependencies" must be validated against a system that cannot predict.

(3) While this study shows that stimulus dependency can account for pre-onset responses, it remains unclear whether this fully explains them, or whether predictive processing still plays a role. The more important question is whether pre-activation remains after accounting for these confounds.

We thank the reviewer for this question, and we agree that the question whether pre-activation occurs is an important and interesting one. However, we ask a different question in our study: Our goal is not to definitively establish whether the brain predicts during language processing; it is to scrutinise what counts as evidence for prediction, and to correct for some highly influential claims made in the literature. The reviewer asks whether pre-activation remains "after accounting for these confounds." But the point we are trying to make is that in this analytical framework, one cannot analytically account for these confounds: corrections to the X matrix leave dependencies in the data itself intact, as the acoustic control demonstrates.

We do offer recommendations for future work. The passive control systems approach can serve as a benchmark: pre-onset neural encoding (or decoding) can only count as evidence for prediction if it exceeds what is observed in a passive control system like acoustics (which is not what we observe). Additionally, the field could move toward less naturalistic stimuli with tighter experimental controls, reducing the correlations that make this attribution so difficult. Developing a new definitive test is beyond the scope of our paper, but we believe applying this benchmark is a necessary first step.

To make this clearer, we have rewritten the Discussion to explicitly state this criterion (lines 331-340) and to outline these recommendations for future work (lines 337-340). We have also added a paragraph extending our argument to decoding approaches (lines 343-354), noting that the same ambiguity applies regardless of analytical direction.

Recommendations for Authors:

Reviewer #1 (Recommendations for Authors):

As per my "Weakness" point, I would appreciate engagement with the conceptual point related to the difference between prediction and stimulus correlations. Most importantly, I hope the authors will spell out more explicitly which predictions their proposal makes, and how exactly those would be present in an encoding model.

Our proposal makes a clear prediction: if pre-onset encoding can be explained by stimulus dependencies (essentially a confound in the analysis) the same hallmarks should emerge in passive control systems that encode the stimulus but do not predict. We test this with word embeddings and speech acoustics, and both show hallmarks despite not doing any prediction.

Reviewer #2 (Recommendations for Authors):

I greatly enjoyed reading the paper and only have minor quibbles. The work is overdue and will no doubt be a valuable addition to the literature to push back on over-hyped claims about the implications of pre-word predictivity in neural response. I have few issues with the methods that the paper uses, they seem sensible and in line with previous work that has investigated these questions, and I did not find typos.

One point I would like to raise is whether or not there is a more effective solution to resolving the issues behind residualization that the paper demonstrates. The authors show that removing next-word information does not effectively resolve the problem that local relationships in the stimulus dataset pose. The challenge to me here seems to be that it is difficult to get a model to "not learn" a relationship that is learnable. I wonder if a better solution to this is to not try to get a model to exclude a set of information but instead to do some sort of variance partitioning where you train a model to predict the next-word representation from the current-word representation (as in the self-predictivity analysis) and then build an encoding model out of the predicted representation. Then, compare the pre-word-onset encoding performance of the prediction with the pre-word-onset encoding performance of the original representation. If the performance of the two models roughly matches, that would be strong evidence that most of what these models are capturing before word onset is just explainable by the stimulus dependencies, no?

We would like to thank the reviewer for their kind words and positive appraisal!

The proposed analysis is that if a linear proxy representation, w_hat_t – predicted linearly from w_{t-1} – yields pre-onset predictivity comparable to the actual w_t vector, this would support that the effect can be explained by stimulus dependencies. While this is an interesting alternative analysis, we would be cautious about the inverse conclusion: that if w_t outperforms the linear proxy w_hat_t, the residual variance must reflect true neural prediction.

This is because of our control system results. We show that even when we remove the "predictable" shared variance – which is similar to computing the difference between w_t and w_hat_t – the unique information still yields pre-onset predictivity, albeit reduced, in the passive acoustics that by definition cannot predict. Therefore, instead of developing an ever-more-clever way to "correct" for the problem by adjusting the X matrix, we focus on showing that the problem lies in the stimulus itself. For the revision, we focused on reframing the problem and hope we have punched a fuller hole in the logic by breaking down the fundamental issue more clearly and showing it applies to the stimulus material of Goldstein et al. (2022) as well.

Additionally, I would say that I was a bit confused about what was going on in the methods figures, to the point where I do not see the value in having them, but thankfully, the text was clear enough to resolve that confusion.

We are sad the methods illustration wasn’t helpful. In presentations we have found that the illustrations were generally helpful to bring the analysis across, e.g. the aspect of keeping the analysis identical but simply replacing the brain data with either word vectors (current Figure 2) and acoustics (current Figure 3). In the revision we have reorganised the schematics slightly, we introduce the acoustics as a control system earlier, to separately introduce residualisation and its insufficiency (Figure 4). We hope this helps

Reviewer #3 (Recommendations for Authors):

(1) My major concern is the extent to which this study offers new insights beyond what was already demonstrated in Goldstein's work. First, the embedding dependency highlighted by the authors seems somewhat expected, given how these embeddings are constructed: GloVe embeddings are based on word co-occurrence statistics, and GPT embeddings are combinations of embeddings of preceding words. More importantly, Goldstein et al. addressed this issue by regressing out neighboring word embeddings. This control was effective, as also confirmed by the current manuscript, and their main results remain. Therefore, the embedding dependency appears to have been properly accounted for in the earlier study.

Building on the previous point, I appreciate the analysis of dependencies across representational domains, which I see as the main novel contribution of this manuscript. I would encourage the authors to explore this aspect more deeply. If I understand correctly, stimulus dependencies may persist even after regressing out neighboring word embeddings due to two potential factors:

(a) Temporal dependencies in embeddings: since the regression of neighbor words is performed at the word level rather than over time, temporal dependency may remain.

(b) Cross-feature dependencies - specifically, correlations between embeddings and acoustic features.

Regarding the first factor, it is not entirely clear to me whether this is a real problem—i.e., whether word-level regression fails to remove temporal dependencies. A simulation could help clarify this and support the argument. While it's not essential, it would be valuable if the authors could propose a method to address this issue, or at least outline it as a direction for future work.

For the second point, it would be helpful for the authors to explicitly explain the potential relationship between word embeddings and acoustic features. Additionally, while correlations between features are a common problem in speech research, they are typically addressed by regressing out acoustic features early in the analysis (Gwilliams et al., 2022). It would strengthen the current findings if the authors could test whether the self-predictability persists even after controlling for neighboring embeddings and acoustic features.

We appreciate the extensive and detailed engagement with our work, which has been very useful in highlighting key unclarities and gaps we had to address.

We do believe our study goes well beyond what was shown by Goldstein, by identifying a fundamental limitation in their analysis, and showing that their purported control analyses do not in fact control for the problem. We’ll address the reviewers' sub-questions in turn.

(i) Why this offers crucial insights beyond Goldstein et al.

While Goldstein et al. indeed addressed embedding dependencies via residualization (or in their case projection), their conclusion relied on the assumption that any neural encoding surviving this "fix" must reflect genuine predictive pre-activation. Our study invalidates this assumption. By applying the residualization fix, we show that the "hallmarks of prediction" persist just as robustly in a passive control system that cannot predict (the speech acoustics) as in the neural data. (We also show this for bigram removal.)

This provides a key new insight: persistent pre-onset predictivity after “correction” is not evidence that the dependency issue was solved. Instead, because the same effect persists in a system that cannot predict (acoustics), the persistence of the hallmarks cannot be attributed to prediction. It demonstrates that the standard "fix" is mathematically insufficient to remove the confound, rendering the original evidence for neural prediction fundamentally ambiguous.

(ii) Why do dependencies/hallmarks persist after residualization?

Residualization successfully removes the linear dependency between the current embedding (w_t) and the previous embedding (w_{t-1}) within the feature space. However, it does not (and cannot) remove the dependency from language itself, and therefore from the brain which (in some format) encodes the linguistic stimulus. Language is massively redundant. Knowing the current word tells you something about what came before – acoustically, syntactically, semantically. As long as the embedding identifies the word, the regression model will re-learn this relationship. For instance, in the case of acoustics, even when using the corrected embedding, the regression will re-learn that certain words (e.g., "Holmes") tend to follow certain acoustic patterns (e.g., the acoustics of "Sherlock"). “This shows that correcting the embeddings is insufficient: the dependencies exist in language itself, and the model will re-learn them from any signal that encodes that language.”

(iii) Why not regress out the acoustics?

This is also why "regressing out acoustics" (as the reviewer suggests) would miss the point. We do not claim that acoustic features leak into the neural signal or that acoustics are a specific confound to be removed. Rather, we use acoustics as a “passive baseline”: a system that encodes the stimulus but cannot predict. That the method yields "hallmarks of prediction" in this baseline demonstrates these hallmarks are not valid evidence for prediction—regardless of what additional features one regresses out. This motivates our proposed criterion: future studies seeing evidence for neural pre-activation should not rest on finding pre-onset encoding per se, since passive systems show this too. Rather, it should require demonstrating that the brain signal contains more information about the upcoming word than the passive stimulus baseline.

As these aspects are fundamental to the interpretation of our study, we have fundamentally re-organised and re-wrote large parts of the paper. We hope it is much clearer now.

(2) To better compare to Goldstein's work, the author may consider performing the same analyses using their publicly available dataset.

This is a good suggestion. When we initially conducted this research, the Goldstein dataset was not yet publicly available. It now is, and we have applied our analyses to their stimulus material. The same problem emerges: the hallmarks of prediction appear in the acoustics of their podcast stimuli. Even after applying the control analyses, pre-onset predictivity is robust in their acoustics (indeed, in correlation terms, higher than reported for the neural data, so there is not more predictivity in the brain than in the stimulus material), confirming that the issue we identify applies to the original dataset. Results are shown in Figures S2B, S3B, S5C, and S6B.

(3) It is also interesting to show the predictability effect after word onsets for self-predictability analyses, for example, in Figure 2C. The predictability effect is not only reflected in pre-onset responses but also in post-onset responses, i.e., larger responses for unpredicted words. Whether the stimulus dependency mirror this effect?

Our paper focuses specifically on temporal dependencies – the capacity of the current word to predict the previous stimulus signal (e.g., previous acoustics, previous embeddings) – and how this mimics neural pre-activation. Post-onset analyses, by contrast, concerns the mapping between the current word and its concurrent signal, which involves fundamentally different mechanisms (e.g., mapping fidelity, frequency effects, acoustic clarity, word length) and would require the consideration of covariates of the attributes of the word post-onset to meaningfully interpret. Post-onset, there can be differences between predictable and non predictable words – e.g. sometimes unpredictable words are pronounced with more emphasis – which is why surprisal studies include a large range of covariates. However, this is not about stimulus dependencies or pre-activation, so we consider it is beyond scope of our study.

(4) The authors might consider reporting the encoding performance for the residual word embeddings, similar to Figure S6B in Goldstein's paper. This would allow us to determine whether pre-activation persists in the MEG responses and compare its pattern with the predictability of pre-onset acoustics.

We do report this analysis, in the revised supplement it is shown in Figure S7. We placed it in the supplement precisely because residualized embeddings are not the "fix" they appear to be: as we show, they still yield strong pre-onset predictivity in the passive acoustic baseline (Figure 4, S6), undermining their use as a control.

(5) The series of previous pre-activation analyses proposed fruitful findings, e.g., the difference between brain regions (Fig. S4, (Goldstein et al., 2022)) and the difference between listeners and speakers (Figure 2, (Zada et al., 2024)). Whether these observed differences can be explained by the stimulus dependency?

We appreciate this question. Our goal is to address the general logic of using pre-onset encoding as evidence for prediction, rather than to critique every finding in specific papers, especially as it pertains to a specific author. But briefly:

Speaker vs. Listener differences (Zada et al., 2024): Zada et al. report distinct temporal profiles: speaker encoding peaks pre-onset (planning?), whereas listener encoding peaks post-onset but shows a pre-onset "ramp." Our critique applies to interpreting this ramp as "prediction." However, this interpretation is not central to their paper, which focuses on speaker-listener coupling via shared embedding spaces. We leave the implications (which are clear enough) to the reader.

Regional differences (Goldstein et al., 2022): Encoding timecourses do vary across electrodes, as we also observe across MEG sources (and participants). But our point is logical: because pre-onset encoding does not necessarily reflect prediction, finding a channel with stronger pre-onset encoding does not mean that channel performs “more prediction”. For instance, one subject in the Armeni dataset showed higher pre-onset than post-onset encoding (and indeed activity) overall – but it would be implausible to conclude this subject "only predicts" and does not “process” or “listen”. More likely, this reflects differences in signal-to-noise, integration windows, or source contributions. The exact sources of these morphological differences are interesting but unclear, and speculating on them is beyond our scope.

(6) I appreciate that the authors have shared their code; however, some parts appear to be missing. For example, the script encoding_analysis.py only includes package-loading code.

Thank you for noticing, we have updated our code database.

(7) What do the error bars in the figures represent - for example, in Figure 1C? How many samples were included in the significance tests? The difference between the two curves appears small, yet it is reported as significant. Additionally, Figure S1 shows large differences between subjects and between the two MEG datasets. Do the authors have any explanation for these differences?

The shaded areas in our previous Figure 1c) show 95% confidence intervals computed over the 100 MEG sources identified to be part of the bilateral language system and the 10 cross-validation splits.

We do not have an elaborate explanation for the differences in encoding performance across the three subjects in the few-subject dataset. Instead, we interpret these differences as a likely consequence of substantial inter-individual variability in evoked responses, even at the source level, arising from differences in cortical folding and the orientation of underlying current dipoles. We deem this a likely explanation since different electrodes in Goldstein’s ECoG data also showed very different encoding profiles.

With respect to the multi-subject dataset, we suspect that the large differences stem most likely from two substantial differences: First, the acoustics were purposefully manipulated by the experimenters to reduce temporal dependence. This made it harder for listeners to concentrate on the stories and thereby might have potentially led to lower quality neural data. Furthermore, it reduced one form of stimulus dependency, namely the acoustic temporal dependencies, which could be exploited by the encoding model to reach higher encoding accuracies. Secondly, MEG has a notoriously poor signal-to-noise ratio, and the amount of data per participant (7.745 words as opposed to 85.719 in the few-subject dataset) might not have been enough to produce reliably high encoding results.

Finally, the current study is clear and convincing, and my suggestions are not intended to question its novelty or robustness. Rather, I believe the authors are in a strong position to address a critical question in language processing: whether pre-activation occurs. The authors have thoughtfully considered important confounds related to pre-onset responses. Adding some approaches to regressing out these confounds could be particularly helpful for determining whether a true pre-onset response remains.

We thank the reviewer again for their constructive feedback, suggestions and questions. To clarify, however, our goal is *not* to definitively attest to whether pre-activation occurs. Our goal is simply to scrutinise a specific method to test for linguistic prediction. This method purports to be an improvement on conventional post-onset (e.g. surprisal-based) methods, as it can directly investigate effects occurring prior to word onset. We have demonstrated fundamental limitations in the underlying logic of this method. We propose passive control systems as baselines against which claims of prediction should be evaluated. Against this baseline, the current evidence does not show unequivocal support for prediction: pre-onset encoding in the brain does not exceed that in the passive control. However, we do not conclude from this that pre-activation does not exist — that would require a different study entirely. Our aim is more methodological: to establish what should count as evidence for prediction, not to settle whether prediction occurs.

We would like to thank the reviewers and editors for their thoughtful feedback, which has been tremendously helpful in improving the paper.

Author response:

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

We sincerely thank the editor and both reviewers for their time and thoughtful feedback on our manuscript. We have carefully addressed all the concerns raised in the responses below and incorporated the suggested revisions into the manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors investigated the population structure of the invasive weed Lantana camara from 36 localities in India using 19,008 genome-wide SNPs obtained through ddRAD sequencing.

Strengths:

The manuscript is well-written, the analyses are sound, and the figures are of great quality.

Weaknesses:

The narrative almost completely ignores the fact that this plant is popular in horticultural trade and the different color morphs that form genetic populations are most likely the result of artificial selection by humans for certain colors for trade, and not the result of natural selfing. Although it may be possible that the genetic clustering of color morphs is maintained in the wild through selfing, there is no evidence in this study to support that. The high levels of homozygosity are more likely explained as a result of artificial selection in horticulture and relatively recent introductions in India. Therefore, the claim of the title that "the population structure.. is shaped by its mating system" is in part moot, because any population structure is in large part shaped by the mating system of the organism, but further misleading because it is much more likely artificial selection that caused the patterns observed.

The reviewer raises the possibility that the observed genetic patterns may have originated through the selection of different varieties by the horticultural industry. While it is plausible that artificial selection can lead to the formation of distinct morphs, the presence of a strong structure between them in the wild populations cannot be explained just based on selection. The observed patterns in the inbreeding coefficient and heterozygosity can indeed arise from multiple factors, including past bottlenecks, selection, inbreeding, and selfing. In the wild, different flower colour variants frequently occur in close physical proximity and should, in principle, allow for cross-fertilization. Over time, this gene flow would be expected to erode any genetic structure shaped solely by past selection. However, our results show no evidence of such a breakdown in structure. Despite co-occurring in immediate proximity, the flower colour variants maintain distinct genetic identities. This suggests the presence of a barrier to gene flow, likely maintained by the species' mating system. Moreover, the presence of many of these flower colour morphs in the native range—as documented through observations on platforms like iNaturalist—suggests that these variants may have a natural origin rather than being solely products of horticultural selection.

While it is plausible that horticultural breeding involved efforts to generate new varieties through crossing—resulting in the emergence of some of the observed morphs—even if this were the case, the dynamics of a self-fertilizing species would still lead to rapid genetic structuring. Following hybridization, just a few generations of selfing are sufficient to produce inbred lines, which can then maintain distinct genetic identities. As discussed in our manuscript, such inbred lines could be associated with specific flower colour morphs and persist through predominant self-fertilization. This mechanism provides a compelling explanation for the strong genetic structure observed among co-occurring flower colour variants in the wild.

To further validate this, we conducted a bagging experiment on Lantana camara inflorescences to exclude insect-mediated cross-pollination. The results showed no significant difference in seed set between bagged and open-pollinated flowers, supporting the conclusion that L. camara is primarily self-fertilizing in India. These results are included in the revised manuscript.

As the reviewer rightly points out, the mating system of a species plays a crucial role in shaping patterns of genetic structure. However, in many natural populations, structuring patterns are often influenced by a combination of factors such as selection, barriers to gene flow, and genetic drift. In some cases, the mating system exerts a more prominent influence at the microgeographic level, while in others, it can shape genetic structure at broader spatial scales. What is particularly interesting in our study is that - the mating system appears to shape genetic structure at a subcontinental scale. Despite the species having undergone other evolutionary forces—such as a genetic bottleneck and expansion due to its invasive nature—the mating system exerts a more pronounced effect on the observed genetic patterns, and the influence of the mating system is remarkably strong, resulting in a clear and consistent genetic structure across populations.

Reviewer #1 (Recommendations for the authors):

Lantana camara is a globally invasive plant as the authors mention in their manuscript, but this study only focuses on India. This should be reflected in the title.

The reviewer has suggested that the title should reflect the study area. Since our sampling covers nearly all regions in India, we believe the patterns observed here are likely representative of those in other parts of the invaded range. For this reason, we would prefer to retain the current heading.

It would be helpful if the pictures of the flowers in Figure 3 were larger to more clearly see the different colors.

As per the reviewers suggestion we have increased the size of the images to improve clarity.

Figure 4 could probably be moved to supplemental material, it does not add much to the results.

We feel it is important to reiterate that the patterns we observe in Lantana are consistent with what one would expect in any predominantly self-fertilizing species. It act as an additional proof and therefore, we believe it is important to retain this figure, as it effectively conveys this link.

Reviewer #2 (Public review):

Summary:

The authors performed a series of population genetic analyses in Lantana camara using 19,008 genome-wide SNPs data from 359 individuals in India. They found a clear population structure that did not show a geographical pattern, and that flower color was rather associated with population structure. Excess of homozygosity indicates a high selfing rate, which may lead to fixation of alleles in local populations and explain the presence of population structure without a clear geographic pattern. The authors also performed a forward simulation analysis, theoretically confirming that selfing promotes fixation of alleles (higher Fst) and reduction in genetic diversity (lower heterozygosity).

Strengths:

Biological invasion is a critical driver of biodiversity loss, and it is important to understand how invasive species adapt to novel environments despite limited genetic diversity (genetic paradox of biological invasion). Lantana camara is one of the hundred most invasive species in the world (IUCN 2000), and the authors collected 359 plants from a wide geographical range in India, where L. camara has invaded. The scale of the dataset and the importance of the target species are the strengths of the present study.

Weaknesses:

One of the most critical weaknesses of this study would be that the output modelling analysis is largely qualitative, which cannot be directly comparable to the empirical data. The main findings of the SLiM-based simulation were that selfing promotes the fixation of alleles and the reduction of genetic diversity. These are theoretically well-reported knowledge, and such findings themselves are not novel, although it may have become interesting these findings are quantitatively integrated with their empirical findings in the studied species. In that sense, a coalescent-based analysis such as an Approximate Bayesian Computation method (e.g. DIY-ABC) utilizing their SNPs data would be more interesting. For example, by ABC-based methods, authors can infer the split time between subpopulations identified in this study. If such split time is older than the recorded invasion date, the result supports the scenario that multiple introductions may have contributed to the population structure of this species. In the current form of the manuscript, multiple introductions were implicated but not formally tested.

Through our SLiM simulations, we aimed to demonstrate that a pattern of strong genetic structure within a location (similar to what we observed in Lantana camara) can arise under a predominantly self-fertilizing mating system. These simulations were not parameterized using species-specific data from Lantana but were intended as a conceptual demonstration of the plausibility of such patterns under selfing using SNP data. While the theoretical consequences of self-fertilisation have been widely discussed, relatively few studies have directly modelled these patterns using SNP data. Our SLiM simulations contribute to this gap and support the notion that the observed genetic structuring in Lantana may indeed result from predominant self-fertilisation. Therefore, we conducted these simulations ourselves for invasive plants to test whether the patterns we observed are consistent with expectations for a predominantly self-fertilising species.

Additionally, as suggested by the reviewer, we have performed demographic history simulations using fastsimcoal2 to investigate the divergence among different flower colour morphs. The results have been incorporated into the revised manuscript.

First, the authors removed SNPs that were not in Hardy-Weinberg equilibrium (HWE), but the studied populations would not satisfy the assumption of HWE, i.e., random mating, because of a high level of inbreeding. Thus, the first screening of the SNPs would be biased strongly, which may have led to spurious outputs in a series of downstream analyses.

Applying a HWE filter is a common practice in genomic data analysis because it helps remove potential sequencing or genotyping artefacts, which can otherwise bias downstream analyses. However, we understand that HWE filtering can also remove biologically informative loci and potentially bias the analysis, especially when a stringent cutoff is used. A strict filter might retain only loci that perfectly fit Hardy–Weinberg expectations and exclude sites influenced by real evolutionary processes like selection and/or inbreeding.

To balance this, we used a mild HWE filter, aiming to remove clear artefacts while retaining loci that may reflect genuine biological signals. Another reason for applying it is that many downstream tools, for example, admixture, assume the markers are neutral and not strongly deviating from HWE (although this assumption may not always hold). This helps in avoiding the complexity of the model.

Second, in the genetic simulation, it is not clear how a set of parameters such as mutation rate, recombination rate, and growth rate were determined and how they are appropriate.

We have cited the references for these values in the manuscript. However, for Lantana, many such baseline data are not available, so we used general values reported for plants, which is an accepted approach when working with understudied species. Moreover, the aim of these simulations was to develop a general understanding of how mating systems influence genetic diversity in invasive plants, rather than to parameterize the simulations specifically for Lantana.

While we acknowledge that this simulation does not provide an exact representation of the species' evolutionary history, the goal of the simulation was not to produce precise estimates but rather to illustrate the feasibility of such strong genetic structuring resulting from self-fertilisation alone.

Importantly, while authors assume the selfing rate in the simulation, selfing can also strongly influence the effective mutation rate (e.g. Nordborg & Donnelly 1997 Genetics, Nordborg 2000 Genetics). It is not clear how this effect is incorporated in the simulation.

In genetic simulations, it is often best to begin with simpler scenarios involving fewer parameters, and we followed this approach. As the reviewer rightly pointed out, selfing can influence multiple factors such as mutation and recombination rates. However, to first understand the broad effects, we chose to work with simpler scenarios where both mutation and recombination rates were kept constant.

Third, while the authors argue the association between flower color and population structure, their statistical associations were not formally tested.

We thank the reviewer for this valuable suggestion. We have performed a MANOVA to test the association between flower colour and genetic structure. These results are incorporated in the revised manuscript.

Also, it is not mentioned how flower color polymorphisms are defined. Could it be possible to distinguish many flower color morphs shown in Figure 1b objectively?

We carefully considered this and defined our criteria based on flower colour. Specifically, we named morphs according to the colour of both young and old flowers. If both stages shared the same colour, we used that colour as the name. As shown in Figure 1b, it is possible to reliably distinguish between the different flower colour morphs. While one could also measure flower colour using a photometer, we believe both approaches yield similar results.

I am concerned particularly because the authors also mentioned that flower color may change temporally and that a single inflorescence can have flowers of different colors (L160).

The flower colour changes within an inflorescence, with young flowers shifting colour after pollination. However, this trend is consistent within a plant; for example, the yellow–pink morph always changes from yellow to pink. Based on this consistency, we incorporated a naming system that considers both the colour of younger and older flowers.

Reviewer #2 (Recommendations for the authors):

Figure 4: Figures a and b are not the "signatures of high inbreeding", because such patterns could also simply happen due to geographical isolation. The title of the figure could be changed. Figure 4c should be presented as a histogram.

We have incorporated this suggestion into the manuscript and revised the figure title accordingly. However, we believe that presenting Figure 4c in its current form is more informative.

L459 "in the introduced range, Lantana is self-compatible": is it self-incompatible in the native range? If it is known, it could be mentioned in the manuscript.

A previous study from India demonstrated that self-fertilisation is possible in Lantana, providing an additional line of evidence for our findings. However, Lantana remains poorly studied in its native range, and to the best of our knowledge, only a single study has examined its pollination biology there, which we have cited in this paper.

Reviewer #1 (Public review):

Summary:

In this paper, Chen et al. identified a role for the circadian photoreceptor CRYPTOCHROME (CRY) in promoting wakefulness under short photoperiods. This research is potentially important as hypersomnolence is often seen in patients suffering from SAD during winter times. The mechanisms underlying these sleep effects are poorly known.

Strengths:

The authors clearly demonstrated that mutations in cry lead to elevated sleep under 4:20 Light-Dark (LD) cycles. Furthermore, using RNAi, they identified GABAergic neurons as a primary site of CRY action to promote wakefulness under short photoperiods. They then provide genetic and pharmacological evidence demonstrating that CRY acts on GABAergic transmission to modulate sleep under such conditions.

Weaknesses:

The authors then went on to identify the neuronal location of this CRY action on sleep. This is where this reviewer is much more circumspect about the data provided. The authors hypothesize that the l-LNvs which are known to be arousal promoting may be involved in the phenotypes they are observing. To investigate this, they undertook several imaging and genetic experiments.

While the authors have made improvements in this resubmitted manuscript, there are still multiple concerns about the paper. I think the authors provide enough evidence suggesting that CRY plays a role in sleep under short photoperiod. The data also supports that CRY acts in GABAergic neurons. However, there are still major issues with the quality of the confocal images presented throughout the paper. In many cases it appears that the images are oversaturated with poor resolution, making it hard to understand what is going on. In addition, none of the drivers used in this study are specific to the neurons the authors aim to manipulate. Therefore, the identity of the GABAergic neurons involved in this CRY dependent sleep mechanism remains unclear. Similarly, whether l-LNvs are the target of this GABA mediated sleep regulation under short photoperiod is not fully demonstrated. The data presented suggests that but does not prove it.

Major concerns:

(1) While the authors provided sleep parameters like consolidation or waking activity for some experiments. These measurements are still not shown for several experiments (for example Figures 2E, 3, 4, 5, and 6). These data are essential, these metrics must be reported for all sleep experiments.

(2) Line 144 "We fed flies with agonists of GABA-A (THIP) and GABA-B receptor (SKF-97541) (Ki and Lim, 2019; Matsuda et al., 1996; Mezler et al., 2001). Both drugs enhance sleep in WT," The proper citation is needed here, Dissel et al., 2015 PMID:25913403. Both THIP and SKF-97541 were used in that paper.

(3) Figure 2C and 2F: it appears that the control data is the same in both panels. That is not acceptable.

(4) Figure 4A: With the quality of the images, it is impossible to assess whether GABA levels are increased at the l-LNvs soma.

(5) Fig 4 S1A shows colabeling of l-LNvs and Gad1-Gal4 expressing neurons. They are almost 100% overlapping signals. This would indicate that the l-LNvs are GABAergic themselves, or that there is a problem with this experiment.

(6) Fig 4 S1B: Again, I can see colabelling of the GFP and PDF staining, suggesting that Gad1-Gal4 expresses in l-LNvs.

(7) Line 184: "Consistently, knocking down Rdl in the l-LNvs rescues the long sleep phenotype of cry mutants (Figure 4-figure supplement 1D)." This statement is incorrect as the driver used for this experiment, 78G01-GAL4 is not specific to the l-LNvs, so it is possible that the phenotypes observed are not coming from these neurons.

(8) Figure 4G-K: None of these manipulations are specific to the l-LNvs. The authors describe 10H10-GAL4 and 78G01-GAL4 as l-LNvs specific tools, but this is not the case. Why not use the SS00681 Split-GAL4 line described in Liang et al., 2017 PMID: 28552314? It is possible that some of the effects reported in this manuscript are not caused by manipulating the l-LNvs.

(9) Similarly for the manipulation of s-LNvs, the authors cannot rule out effect that are coming from other cells as R6-GAL4 is not specific to s-LNvs.

(10) The staining presented in Fig 5 S1 is not very convincing. Difficult to see whether Gad1-GAL4 only expresses in the s-LNvs.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this paper, Chen et al. identified a role for the circadian photoreceptor CRYPTOCHROME (cry) in promoting wakefulness under short photoperiods. This research is potentially important as hypersomnolence is often seen in patients suffering from SAD during winter times. The mechanisms underlying these sleep effects are poorly known.

Strengths:

The authors clearly demonstrated that mutations in cry lead to elevated sleep under 4:20 Light-Dark (LD) cycles. Furthermore, using RNAi, they identified GABAergic neurons as a primary site of cry action to promote wakefulness under short photoperiods. They then provide genetic and pharmacological evidence demonstrating that cry acts on GABAergic transmission to modulate sleep under such conditions.

Weaknesses:

The authors then went on to identify the neuronal location of this cry action on sleep. This is where this reviewer is much more circumspect about the data provided. The authors hypothesize that the l-LNvs which are known to be arousal-promoting may be involved in the phenotypes they are observing. To investigate this, they undertook several imaging and genetic experiments.

Major concerns:

(1) Figure 2 A-B: The authors show that knocking down cry expression in GABAergic neurons mimics the sleep increase seen in cryb mutants under short photoperiod. However, they do not provide any other sleep parameters such as sleep bout numbers, sleep bout duration, and more importantly waking activity measurements. This is an essential parameter that is needed to rule out paralysis and/or motor defects as the cause of increased "sleep". Any experiments looking at sleep need to include these parameters.

Thank you for bringing up these points. We have now included these sleep parameters in Figure 2—figure supplement 3.

(2) For all Figures displaying immunostaining and imaging data the resolution of the images is quite poor. This makes it difficult to assess whether the authors' conclusions are supported by the data or not.

We apologize for the poor resolution. This is probably due to the compression of the figures in the merged PDF file. We are now uploading the figures individually and hopefully this can resolve the resolution issue.

(3) In Figure 4-S1A it appears that the syt-GFP signal driven by Gad1-GAL4 is colabeling the l-LNvs. This would imply that the l-LNvs are GABAergic. The authors suggest that this experiment suggests that l-LNvs receive input from GABAergic neurons. I am not sure the data presented support this.

We agree that this piece of data alone is not sufficient to demonstrate that the l-LNvs receive GABAergic inputs rather than the l-LNvs are GABAergic. However, when nlsGFP signal is driven by two independent Gad1-GAL4 lines (one generated by P element insertion while the other generated by GAL4 inserted into the Gad1 locus), we do not observe any prominent signal in the l-LNvs (Figure 5A and B; Figure 5-figure supplement 1A). We have also co-labeled using Gad1GAL4 and PdfLexA (Figure 5-figure supplement 1B). As can be seen, Gad1GAL4-driven GFP signal is present only in the s-LNvs but not the l-LNvs. This further supports the idea that the l-LNvs are not GABAergic, and that the syt-GFP signal likely arises from GABAergic neurons projecting to the l-LNvs.

(4) In Figure 4-S1B. The GRASP experiment is not very convincing. The resolution of the image is quite poor. In addition, the authors used Pdf-LexA to express the post t-GRASP construct in l-LNvs, but Pdf-LexA also labels the s-LNvs, so it is possible that the GRASP signal the authors observe is coming from the s-LNvs and not the l-LNvs. The authors could use a l-LNvs specific tool to do this experiment and remove any doubts. Altogether this reviewer is not convinced that the data presented supports the conclusion "All in all, these results demonstrate that GABAergic neurons project to the l-LNvs and form synaptic connections." (Line 176). In addition, the authors could have downregulated the expression of Rdl specifically in l-LNvs to support their conclusions. The data they are providing supports a role for RDL but does not prove that RDL is involved in l-LNvs.

Thank you for these wonderful suggestions. Again we apologize for the poor resolution and hopefully by uploading the images separately we can resolve this issue. We agree that the GRASP signal could be coming from the s-LNvs and not the l-LNvs but unfortunately we are not able to find a LexA that is specifically expressed in the l-LNvs. We believe the trans-Tango data further support the idea that GABAergic neurons project to and form synaptic connections with the l-LNvs. Nonetheless, we have changed our conclusion to “All in all, these results strongly suggest that GABAergic neurons project to the l-LNvs and form synaptic connections” to be more rigorous. In addition, we have obtained R78G01GAL4 which is specifically expressed in the l-LNvs, and using this GAL4 to knock down Rdl rescues the long-sleep phenotype of cry mutants (Figure 4—figure supplement 1D).

(5) In Figures 4 A and C: it appears that GABA is expressed in the l-LNvs. Is this correct? Can the authors clarify this? Maybe the authors could do an experiment where they co-label using Gad1-GAL4 and Pdf-LexA to clearly demonstrate that l-LNvs are not GABAergic. Also, the choice of colors could be better. It is very difficult to see what GABA is and what is PDF.

Thank you for this wonderful suggestion. We have now co-labeled using Gad1GAL4 and PdfLexA (Figure 5-figure supplement 1B). As can be seen, Gad1GAL4-driven GFP signal is present only in the s-LNvs but not the l-LNvs. We suspect the GABA signal at the l-LNvs may arise from the GABAergic projections received by these cells. We have now changed the color of the GABA/PDF signals in these images and have reduced the intensity of the PDF signal. Hopefully, it would be easier to visualize in this revised version.

(6) Figure 4G: Pdf-GAL4 expresses in both s-LNvs and l-LNvs. So, in this experiment, the authors are silencing both groups, not only the l-LNvs. Why not use a l-LNvs specific tool?

Thank you for bring up this important point. We have previously used c929GAL4 to express Kir2.1 and this led to lethality. We have now used two l-LNv-specific GAL4 drivers (R78G01GAL4 and R10H10GAL4) that we newly obtained to express Kir2.1 but did not observe significant effect on sleep. Please see Author response image 1 for the results.

Author response image 1.

Daily sleep duration of male flies expressing Kir2.1 in l-LNvs using R78G01GAL4 (A)(n = 40, 41, 30 flies) and R10H10GAL4 (B) (n = 40, 41, 32 flies) and controls, monitored under 4L20D. One-way ANOVA with Bonferroni multiple comparison test was used to calculate the difference between experimental group and control group.

(7) Figure 4H-I: The C929-GAL4 driver expresses in many peptidergic neurons. This makes the interpretation of these data difficult. The effects could be due to peptidergic cells being different than the l-LNvs. Why not use a more specific l-LNvs specific tool? I am also confused as to why some experiments used Pdf-GAL4 and some others used C929-GAL4 in a view to specifically manipulate l-LNvs? This is confusing since both drivers are not specific to the l-LNvs.

Thank you for bring up these important points. We have now used the l-LNv-specific R10H10GAL4 and the results are more or less comparable with that of c929GAL4 (Figure 4I and K), i.e. activating the l-LNvs blocks the long-sleep phenotype of cry mutants. The reason PdfGAL4 is used in 4G is because c929GAL4 leads to lethality while the l-LNv-specific GAL4 lines do not alter sleep.

(8) Figure 5-S1B: Why does the pdf-GAL80 construct not block the sleep increase seen when reducing expression of cry in Gad1-GAL4 neurons? This suggests that there are GABAergic neurons that are not PDF expressing involved in the cry-mediated effect on sleep under short photoperiods.

Yes, this is indeed the conclusion we draw from this result, and we commented on this in the Discussion: “Moreover, inhibiting cry RNAi expression in PDF neurons does not eliminate the long-sleep phenotype of Gad1GAL4/UAScryRNAi flies. Therefore, we suspect that cry deficiency in other GABAergic neurons is also required for the long-sleep phenotype. Given that the s-LNvs are known to express CRY and appear to be GABAergic based on our findings here, we believe that CRY acts at least in part in the s-LNvs to promote wakefulness under short photoperiod.”

In conclusion, it is not clear that the authors demonstrated that they are looking at a cry-mediated effect on GABA in s-LNvs resulting in a modulation of the activity of the l-LNvs. Better images and more-suited genetic experiments could be used to address this.

Thank you very much for all the comments. They are indeed quite helpful for improving our manuscript. Hopefully, with images of higher quality and the additional experiments described above, we have now provided more evidence supporting our major conclusion.

Reviewer #2 (Public Review):

Summary:

The sleep patterns of animals are adaptable, with shorter sleep durations in the winter and longer sleep durations in the summer. Chen and colleagues conducted a study using Drosophila (fruit flies) and discovered that a circadian photoreceptor called cryptochrome (cry) plays a role in reducing sleep duration during day/night cycles resembling winter conditions. They also found that cry functions in specific GABAergic circadian pacemaker cells known as s-LNvs inhibit these neurons, thereby promoting wakefulness in the animals in the winter. They also identified l-LNvs, known as arousal-promoting cells, as the downstream neurons.

Strengths:

Detailed mapping of the neural circuits cry acts to mediate the shortened sleep in winter-like day/night cycles.

Weaknesses:

The supporting evidence for s-LNvs being GABAergic neurons is not particularly strong. Additionally, there is a lack of direct evidence regarding changes in neural activity for s-LNvs and l-LNvs under varying day/night cycles, as well as in cry mutant flies.

Thank you very much for all the comments. We have now expressed nlsGFP by two independent Gad1-GAL4 lines (one generated by P element insertion while the other generated by GAL4 inserted into the Gad1 locus), and positive signals in the s-LNvs can be observed (Figure 5A and B; Figure 5-figure supplement 1A). Hopefully, this can provide some further support regarding the s-LNvs being GABAergic neurons.

We have now examined GCaMP signals in the l- and s-LNvs of WT and cry mutants under 4L20D/12L12D. Please see Author response image 2 for the results. As can be seen, both WT and cry mutants show photoperiod-dependent changes. Interestingly, cry mutants show more prominent reduction of GCaMP signal in the l-LNvs compared to WT under 12L12D vs. 4L20D, but the sleep duration phenotype is observed only under 4L20D. Moreover, GCaMP signal is elevated in the s-LNvs of cry mutants relative to WT under 4L20D but decreased under 12L12D. These results indicate that there are distinct mechanisms regulating sleep under short vs. normal photoperiod (with CRY being dispensable under 12L12D), and the role of CRY in modulating the activity of these neurons are also photoperiod-dependent. Further in-depth characterizations are need to delineate these complex issues.

Author response image 2.<br /> Quantification of GCaMP6m signal intensity normalized to that of tdTomato under 12L12D and 4L20D (n = 25-45 cells). Student’s t-test: compared to WT, #P < 0.05, ##P < 0.01; 12L12D vs. 4L20D, *P < 0.05, ***P < 0.001.

Reviewer #3 (Public Review):

Summary:

In humans, short photoperiods are associated with hypersomnolence. The mechanisms underlying these effects are, however, unknown. Chen et al. use the fly Drosophila to determine the mechanisms regulating sleep under short photoperiods. They find that mutations in the circadian photoreceptor cryptochrome (cry) increase sleep specifically under short photoperiods (e.g. 4h light: 20 h dark). They go on to show that cry is required in GABAergic neurons. Further, they suggest that the relevant subset of GABAergic neurons are the well-studied small ventral lateral neurons that they suggest inhibit the arousal-promoting large ventral neurons via GABA signalling.

Strengths:

Genetic analysis to show that cryptochrome (but not other core clock genes) mediates the increase in sleep in short photoperiods, and circuit analysis to localise cry function to GABAergic neurons.

Weaknesses:

The authors' conclusion that the sLNvs are GABAergic is not well supported by the data. Better immunostaining experiments and perhaps more specific genetic driver lines would help with this point (details below).

(1) The sLNvs are well known as a key component of the circadian network. The finding that they are GABAergic would if true, be of great interest to the community. However, the data presented in support of this conclusion are not convincing. Much of the confocal images are of insufficient resolution to evaluate the paper's claims. The Anti-GABA immunostaining in Fig 4 and 5 seem to have a high background, and the GRASP experiments in Fig 4 supplement 1 low signal.

We apologize for the poor resolution. This is probably due to the compression of the figures in the merged PDF file. We are now uploading the figures individually and hopefully this can resolve the resolution issue. Unfortunately, the GABA immunostaining does not work very well in our hands and thus the background is high. We have now adjusted the images by changing the minimum lookup table (LUT) value in the green channel to 213, which removes all pixels below 213. This can remove background without changing the gray values, so the analysis is not affected. We have modified all images the exact same way and hopefully this can improve the contrast. Furthermore, we have now expressed nlsGFP by two independent Gad1-GAL4 lines (one generated by P element insertion while the other generated by GAL4 inserted into the Gad1 locus), and positive signals in the s-LNvs can be observed (Figure 5A and B; Figure 5-figure supplement 1A). Hopefully, this can provide some further support regarding the s-LNvs being GABAergic neurons.

Transcriptomic datasets are available for the components of the circadian network (e.g. PMID 33438579, and PMID 19966839). It would be of interest to determine if transcripts for GAD or other GABA synthesis/transport components were detected in sLNvs. Further, there are also more specific driver lines for GAD, and the lLNvs, sLNVs that could be used.

Thank you for these wonderful suggestions. Based on PMID 19966839, both the s-LNvs and l-LNvs express Gad1 and VGAT at a relatively low level, although here in our study Gad1GAL4 expression is observed only in the s-LNvs and not l-LNvs. We have commented on this in the 4th paragraph of Discussion: “One study using cell-type specific gene expression profiling demonstrates Gad1 and VGAT expression in both s-LNvs and l-LNvs, although with relatively low signal (Nagoshi et al., 2010). Here we observed that Gad1GAL4 is expressed in the s-LNvs, and their GABA intensity is reduced when we use R6GAL4 to knock down VGAT in these cells.” PMID 33438579 does not report expression of these genes in either s-LNvs or l-LNvs, likely due to insufficient sequencing depth. Furthermore, we have now used two l-LNv-specific GAL4 lines (R78G01GAL4 and R10H10GAL4) to conduct some of the experiments that we previously used c929GAL4 for, and obtained comparable results (Figure 4I and K).

(2) The authors' model posits that in short photoperiods, cry functions to suppress GABA secretion from sLNvs thereby disinhibiting the lNVs. In Fig 4I they find that activating the lLNvs (and other peptidergic cells) by c929>NaChBac in a cryb background reduces sleep compared to activating lLNVs in a wild-type background. It's not clear how this follows from the model. A similar trend is observable in Fig 4H with TRP-mediated activation of lNVs, although it is not clear from the figure if the difference b/w cryb vs wild-type background is significant.

Thank you for bring up this important point. This does appear to be counterintuitive. We suspect that in cry mutants, there is more inhibition occurring at the l-LNvs and thus the system may be particularly sensitive to their activation. Therefore, activating these neurons on the mutant background can result in a more prominent wake-promoting effect compared to that of WT.

Recommendations for the authors:

Our major concern centers around the claim that the sLNvs are GABAergic and secrete GABA onto the lLNVs. As it stands, this is not well supported by the data.

The authors could substantiate these findings by using more specific driver lines for GAD / vGAT (MiMic based lines are available that should better recapitulate endogenous expression). Transcriptomic data for circadian neurons are available, the FlyWire consortium also predicts neurotransmitter identities for specific neural circuits. These datasets could be mined for evidence to support the claim of sLNvs being GABAergic

Thank you for these wonderful suggestions. We have now used MiMic-based lines for Gad1 (BS52090, Mi{MIC}Gad1MI09277) and VGAT (BS23022, Mi{ET1}VGATMB01219) to knock down cry but unfortunately were not able to observe changes in sleep. Please see Author response image 3 for the results.

Author response image 3.

Daily sleep duration of male flies with cry knocked down in GABAergic neurons by Gad1GAL4 (A) (n = 30, 38, 50, 18, 31 flies) or VGATGAL4 (B) (n = 28, 38, 50, 18, 30 flies) monitored under 4L20D.One-way ANOVA with Bonferroni multiple comparison test: compared to UAS control, ###P < 0.001.

Furthermore, we have now included another Gad1GAL4 line which is generated by knocking GAL4 transgene into the Gad1 locus. We are also able to observe increased sleep when using this GAL4 to knock down cry, and positive signals in the s-LNvs can be observed when using this GAL4 to drive nlsGFP (Figure 2B; Figure 5-figure supplement 1A).

Based on PMID 19966839, both the s-LNvs and l-LNvs express Gad1 and VGAT at a relatively low level, although here in our study Gad1GAL4 expression is observed only in the s-LNvs and not l-LNvs. We have commented on this in the 4th paragraph of Discussion: “One study using cell-type specific gene expression profiling demonstrates Gad1 and VGAT expression in both s-LNvs and l-LNvs, although with relatively low signal (Nagoshi et al., 2010). Here we observed that Gad1GAL4 is expressed in the s-LNvs, and their GABA intensity is reduced when we use R6GAL4 to knock down VGAT in these cells.” The FlyWire does not have prediction for this particular circuit that we are interested in.

Further, many of the immunostaining images have high background / low signal - so better confocal images would help, as would the use of more specific driver lines for the lNVs as it is sometimes hard to distinguish the lLNvs from sLNvs.

We have now adjusted all images by changing the minimum lookup table (LUT) value in the green channel to 213 and that of the red channel to 279, which removes all pixels below 213 and 279, respectively. This can remove background without changing the gray values, so the analysis is not affected. We have modified all images the exact same way and hopefully this can improve the signal to noise ratio. We were not able to find a LexA line that is specifically expressed in the l-LNvs but we have found two l-LNv-specific GAL4 lines (R78G01GAL4 and R10H10GAL4). We used these lines to conduct some of the experiments that we previously used c929GAL4 for, and obtained comparable results (Figure 4I and 4K).

Additional specific comments are in the reviews above.

Minor points:

(1) Line 55: CRYPTOCHROME is misspelled.

This has been fixed.

(2) Line 140: The authors need to provide the appropriate references for the use of THIP and SKF-97541.

This has been added.

(3) Line 149: there are multiple GABA-A receptors in flies, the authors should acknowledge that. What about LccH3 or Grd?

Thank you for bring up this important point. Here we focused only on Rdl because it is the only GABA-A receptor known to be involved in sleep regulation. We have modified our description regarding this issue: “We tested for genetic interaction between cry and Resistant to dieldrin (Rdl), a gene that encodes GABA-A receptor in flies and has previously been shown to be involved in sleep regulation.”

1

Reviewer #2 (Public review):

Summary:

This study presents LUNA, an autofocus method that compensates for focus drift during rapid temperature changes. Using this approach, the authors show that E. coli cells continue to grow and divide during cold shock, revealing a coordinated, multi-phase adaptation process that could not be deduced from traditional population measurements. They propose a scattering-theory-based model that reconciles the paradox between growth differences of the bacteria at the single-cell level vs population level.

Strengths:

(1) The LUNA approach is pretty creative, turning coma aberration from what is normally a nuisance into an exploit. LUNA enabled long-term single-cell imaging during rapid temperature downshifts.

(2) The authors show that the long-assumed growth arrest during cold shock from population-level measurements is misleading. At the single-cell level, bacteria do not stop growing or dividing but undergo a continuous, three-phase adaptation process. Importantly, this behavior is highly synchronized across the population and not based on bet-hedging.

(3) Finally, the authors propose a model to resolve a long-standing paradox between single-cell vs population behavior: if cells keep growing, why does optical density (OD) of the culture stop increasing? Using light-scattering theory, they show that OD depends not only on cell number but also on cell volume, which decreases after cold shock. As a result, OD can remain flat, or even decrease, despite continued biomass accumulation. This demonstrates that OD is not a reliable proxy for growth under non-steady conditions.

Weaknesses:

(1) While the authors theoretically explain the advantages of LUNA over existing autofocus methods, it is unclear whether practical head-to-head comparisons have been performed, apart from the comparison to Nikon PFS shown in Video S1. As written, the manuscript gives the impression that only LUNA can solve this problem, but such a claim would require more systematic and rigorous benchmarking against alternative approaches.

(2) No mutants/inhibitors used to test and challenge the proposed model.

(3) Cells display a high degree of synchronization, but they are grown in confined microfluidic channels under highly uniform conditions. It is unclear to what extent this synchrony reflects intrinsic biology versus effects imposed by the microfluidic environment.

(4) To further test and generalize the model, it would be informative to also examine bacterial responses at intermediate temperatures rather than focusing primarily on a single cold-shock condition.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors developed a new autofocusing method, LUNA (Locking Under Nanoscale Accuracy), to address severe focus drift-a major challenge in time-lapse microscopy. Using this method, they tackle a fundamental question in bacterial cold shock response: whether cells halt growth and division following an abrupt temperature downshift. Overall, the experimental design, modeling, and data analysis are solid and well executed. However, several points require clarification or further support to fully substantiate the authors' conclusions.

Strengths:

(1) The LUNA method outperforms existing autofocusing systems with nanoscale precision over a large focusing range. The focusing time is reasonable for the presented experiments, and the authors note potential improvements by using faster motors and optimized control algorithms, suggesting broad applicability. The theoretical simulations and experimental validation provide solid support for the robustness of the method.

(2) Using LUNA, the authors address a long-standing question in bacterial physiology: whether cells arrest growth and division after an abrupt cold shock. Single-cell analyses monitoring the entire course of cold adaptation and steady-state growth reveal features that are obscured in bulk-culture studies: cells continue to grow at reduced rates with smaller cell sizes, resulting in an apparently unchanged population-level OD. The experiments are well designed and analyses are generally solid and largely support the authors' conclusions.

(3) The authors also propose a model describing how population-level OD measurements depend on cell dry mass density, volume, and concentration. This provides a valuable conceptual contribution to the interpretation of OD-based growth measurements, which remain a gold-standard method in microbiology.

We thank the reviewer for acknowledging the strengths of our study.

Weaknesses:

(1) It is unclear whether the author's model explaining the population-level OD during acclimation is broadly applicable. Most analyses focus on a shift from 37˚C to 14˚C, where the model agrees well with experimental data. However, in the 37˚C to 12˚C experiment, OD600 decreases after cold shock (Fig. 5e), and the computed OD does not match the experimental measurements (Fig. S16a). Although the authors attribute this discrepancy to a "complicated interplay," no further explanation is provided, which limits confidence in the model's general applicability.

Thank you for this careful evaluation regarding the model generality. In the experiment with a temperature shift from 37°C to 12°C, the measured OD600 values were 0.243 at 0 hours and 0.242 at 5 hours. In comparison, our model-computed OD600 values were 0.243 at 0 hours and 0.271 at 5 hours. The absolute difference between the measured and computed values at 5 hours is therefore 0.028.

Given the typical experimental variability in OD600 measurements and the limited linear range of the OD-to-biomass approximation (generally considered reliable below ~0.5), this deviation is quantitatively modest. We appreciate your valuable feedback and are happy to provide further clarification if needed.

(2) The manuscript proposes that cell-cycle progression becomes synchronized across the population after cold shock, but the supporting evidence is not fully convincing. If synchronization refers primarily to the uniform reduction in growth rate following cold shock, this could plausibly arise from global translation inhibition affecting all cells. However, the additional claim that "cells encountering a relatively late CSR will accelerate division to maintain synchronization" is not strongly supported by the presented data.

We appreciate your critical reading, which has helped us identify ambiguities in our terminology and strengthen the clarity of our work. Regarding the term “synchronization”, we would like to clarify that it refers to two different scenarios: (i) the synchrony in the timing of growth rate changes after cold shock. The cells initiate the slowdown in growth almost simultaneously, suggesting a highly coordinated, non-stochastic population-level response to cold shock; (ii) the synchrony in division cycle progression.

In the sentence you referenced “cells encountering a relatively late CSR will accelerate divisions to maintain synchronization”, we intended to describe that cells maintain consistent progression of the division cycle after cold shock, meaning that after the same number of elapsed cycles, different cells are at a similar stage in their division timing (Figure 4f, 4g, Figure S14). The term “accelerate” refers to our observation that cells which complete a given cycle later than others tend to have shorter subsequent inter-division intervals, thereby “catching up” to maintain alignment in cycle number across the population. We acknowledge that using “synchronization” in this scenario may be ambiguous, and we will replace it with more precise phrasing “progression of division cycle” to accurately convey this finding.

(3) Several technical terms used in the method development section are not clearly defined and may be unfamiliar to a broad readership, which makes it difficult to fully understand the methodology and evaluate its performance. Examples include depth of focus, focusing precision, focusing time, focusing frequency, and drift threshold value. In addition, the reported average focusing time per location (~0.6 s) lacks sufficient context, limiting the reader's ability to assess its significance relative to existing autofocusing methods.

Thank you for your valuable comments and suggestions. In response, we have added more detailed descriptions in the Methods section of the revised version.

The reviewer noted that the reported average focusing time (~0.6 s) lacks sufficient context, which may limit readers’ ability to assess its significance relative to existing autofocusing methods. We would like to clarify that the core innovation of this work lies in the proposed theoretical framework for autofocusing, which offers advantages over existing methods in terms of focusing precision and range. While focusing time is a practically relevant performance metric, it is primarily presented here as an implementation-dependent parameter rather than a central theoretical contribution of this study. In our experimental setup, an average focusing time of 0.6 s proved sufficient for routine timelapse imaging in microscopy, thereby demonstrating the practical usability of LUNA.

Reviewer #2 (Public review):

Summary:

This study presents LUNA, an autofocus method that compensates for focus drift during rapid temperature changes. Using this approach, the authors show that E. coli cells continue to grow and divide during cold shock, revealing a coordinated, multi-phase adaptation process that could not be deduced from traditional population measurements. They propose a scattering-theory-based model that reconciles the paradox between growth differences of the bacteria at the single-cell level vs population level.

Strengths:

(1) The LUNA approach is pretty creative, turning coma aberration from what is normally a nuisance into an exploit. LUNA enabled long-term single-cell imaging during rapid temperature downshifts.

(2) The authors show that the long-assumed growth arrest during cold shock from population-level measurements is misleading. At the single-cell level, bacteria do not stop growing or dividing but undergo a continuous, three-phase adaptation process. Importantly, this behavior is highly synchronized across the population and not based on bet-hedging.

(3) Finally, the authors propose a model to resolve a long-standing paradox between single-cell vs population behavior: if cells keep growing, why does optical density (OD) of the culture stop increasing? Using light-scattering theory, they show that OD depends not only on cell number but also on cell volume, which decreases after cold shock. As a result, OD can remain flat, or even decrease, despite continued biomass accumulation. This demonstrates that OD is not a reliable proxy for growth under non-steady conditions.

We thank the reviewer for acknowledging the strengths of our study.

Weaknesses:

(1) While the authors theoretically explain the advantages of LUNA over existing autofocus methods, it is unclear whether practical head-to-head comparisons have been performed, apart from the comparison to Nikon PFS shown in Video S1. As written, the manuscript gives the impression that only LUNA can solve this problem, but such a claim would require more systematic and rigorous benchmarking against alternative approaches.

Thank you for your insightful comment regarding the comparison of LUNA with other autofocus methods.

In our study, we primarily compared LUNA with the Nikon PFS system (as shown in Video S1) because Nikon PFS is one of the most widely used commercial autofocus systems in single-cell time-lapse imaging, and its manufacturer provides well-defined performance parameters (e.g., focusing precision within 1/3 depth-of-focus, response time <0.7 s), which facilitates a quantitative comparison. For other commercial systems, such as Olympus ZDC, Zeiss Definite Focus, Leica AFC, and ASI CRISP, the publicly available specifications are often less clearly defined, or are measured under inconsistent conditions, making a direct head-to-head comparison challenging and potentially misleading. Additionally, in our preliminary experiments, we also tested an Olympus microscope and observed severe focus drift during slow cooling processes. From a physical perspective, LUNA is specifically designed to meet the demanding requirements of single-cell experiments, including a wide focusing range and high precision, while existing commercial systems may not physically achieve the combination of range and accuracy needed for such extreme conditions.

(2) No mutants/inhibitors used to test and challenge the proposed model.

We agree that such approaches would provide valuable mechanistic insights and further strengthen the validation of the model presented in this study. In the current work, our primary goal was to introduce LUNA autofocusing method and demonstrate its capability to resolve bacterial cold shock response at the single-cell level with unprecedented precision. As such, we focused on characterizing the wild-type physiological dynamics under cold shock, which already revealed several previously unreported phenomena. We acknowledge that the use of genetic mutants or chemical inhibitors targeting specific cold shock proteins or regulatory pathways would be a logical and powerful next step to dissect the underlying molecular mechanisms and test the causality of the observed growth dynamics. We plan to address this in future work by incorporating such perturbations to further test and refine the model.

(3) Cells display a high degree of synchronization, but they are grown in confined microfluidic channels under highly uniform conditions. It is unclear to what extent this synchrony reflects intrinsic biology versus effects imposed by the microfluidic environment.

The reviewer raises a pertinent question regarding whether the observed high degree of cell synchronization represents an intrinsic biological phenomenon or an artifact induced by the microfluidic environment.

Over the past decade, microfluidic chips, including the specific design used in our work, have become a widely accepted and powerful tool in microbial physiology research. A broad consensus has emerged within the community that the microenvironment within these microchannels does not significantly interfere with or perturb the natural physiological behavior of microorganisms (Dusny, C. & Grünberger, Curr Opin Biotechnol. 63, 26-33 (2020)). This understanding is also supported by the fact that key findings obtained with microfluidic single-cell technologies are reproducible by other methods. For example, the adder model of cell-size homeostasis in E. coli firstly observed in microfluidic chips has been repeatedly validated by different methods (Taheri-Araghi, S. et al. Curr. Biol. 25, 385-391 (2015)). Therefore, while we acknowledge the importance of considering environmental effects, we are confident that the synchronization we report reflects the genuine biological dynamics of E. coli cells.

(4) To further test and generalize the model, it would be informative to also examine bacterial responses at intermediate temperatures rather than focusing primarily on a single cold-shock condition.

We thank the reviewer for this thoughtful suggestion. In designing our experiments, we aimed to study the bacterial cold shock response at the single-cell level. A key feature of this response is that it is typically triggered only when the temperature drops below a certain threshold within a short time duration. We therefore chose to lower the temperature from 37 °C to 14 °C as rapidly as possible. This approach allowed us to leverage the unique capabilities of LUNA while also providing an opportunity to explore this biological process in greater detail.

We agree that investigating bacterial responses across intermediate temperatures would be highly informative for understanding how temperature changes affect cellular physiology. However, this direction addresses a distinct scientific question that lies beyond the scope of the current work. We fully acknowledge its value and do have the intention to explore it in future studies.

Author response:

(1) Claim regarding NNDSVD initialization

Reviewer #1:

The authors state that "MPS is the first implementation of Constrained Non-negative Matrix Factorization (CNMF) with Nonnegative Double Singular Value Decomposition (NNDSVD) initialization." However, NNDSVD initialization is the default method in scikit-learn's NMF implementation and is also used in CaIMAN. I recommend rephrasing this claim in the abstract to more accurately reflect MPS's novelty, which appears to lie in the specific combination of constrained NMF with NNDSVD initialization, rather than being the first use of NNDSVD initialization itself.

We agree that our original phrasing was too broad. NNDSVD-family initialization is widely used in NMF implementations (e.g., scikit-learn) and is available within some pipeline components. We revised the abstract and main text to clarify our intended contribution: MPS seeds CNMF directly with NNDSVD-derived nonnegative factors as the primary initialization strategy, rather than relying on heuristic or greedy ROI-based seeding, integrated within a memory-efficient, end-to-end workflow for long-duration miniscope recordings.

(2) Installation issue on macOS

Reviewer #1:

At present, there are practical issues that limit the usability of the software. The link to the macOS installer on the documentation website is not functional. Furthermore, installation on a MacBook Pro was unsuccessful, producing the following error: "rsync(95755): error: ... Permission denied ...unexpected end of file."

We thank the reviewer for identifying the broken installer link and the macOS installation error. We fixed the macOS installer link on the documentation website and updated installation instructions to explicitly address common macOS permission-related failures (including rsync "Permission denied" errors that arise when attempting to write into protected directories without appropriate privileges). We re-tested installation on clean macOS systems and confirmed successful installation under the revised instructions.

(3) Validation, benchmarking, and cross-pipeline comparison

Reviewer #2:

A major limitation of this manuscript is that the authors don't validate the accuracy of their source extraction using ground-truth data or any benchmark against existing pipelines... Without this kind of validation, it is impossible to truly determine whether MPS produces biologically acceptable results... Considering one of the main benefits of MPS is its low memory demand and ability to run on unsophisticated hardware, the authors should include a figure that shows how processing times and memory usage scale with dataset sizes and differing pipelines... runtime comparisons on identical datasets processed through MPS, CaImAn, Minian, or CaliAli would be necessary to substantiate performance claims of MPS being "10-20X faster".

We thank the reviewers for their careful reading and for raising the question of biological validity, which we agree is central to any calcium imaging analysis tool. We would like to clarify, however, that MPS does not introduce a novel source extraction algorithm, and therefore the question of biological validity is not one that MPS alone can answer - nor should it be expected to. MPS is built on CNMF, the same mathematical framework underlying CaImAn and Minian. The contribution of MPS lies in its initialization strategy and parallelization architecture, which allow this proven framework to operate in the multi-hour recording regime.

To address the reviewers' request for a direct qualitative comparison, we will run MPS, CaImAn, Minian, and MIN1PIPE on a representative 10-minute real recording with clearly visible neurons. The figure will show the spatial components (ROI footprints) and representative temporal traces (ΔF/F) for all four pipelines on identical data. We anticipate that the spatial layouts and temporal dynamics will be highly concordant across pipelines, demonstrating that MPS produces biologically consistent output. We believe this side-by-side comparison will provide a clear demonstration that MPS output is comparable in quality to established tools on tractable recordings.

Regarding runtime comparison across pipelines, we will provide a table showing approximate processing times at three recording durations (5, 20, and 180 minutes). On short recordings, all pipelines are expected to complete successfully at different rates, whereas on long-duration recordings, this pipeline behavior is expected to diverge. We acknowledge that any single runtime benchmark reflects specific hardware and dataset characteristics and may not generalize to all configurations. We will therefore present these data as illustrative rather than definitive and will direct readers to the MPS documentation for guidance on hardware-specific tuning.

(4) Dataset description and scope of generalizability

Reviewer #2:

The current datasets used for validating MPS are not described in the manuscript. The manuscript appears to have 28 sessions of calcium imaging, but it is unclear if this is a single cohort or even animal, or whether these data are all from the same brain region. Importantly, the generalizability of parameter choices and performance could vary for others based on brain region differences, use of alternative calcium indicators...

We agree that the dataset description should be centralized and unambiguous. We added a dedicated Methods subsection stating that all results are based on a single, controlled experimental dataset consisting of 28 long-duration miniscope sessions acquired under consistent conditions (same brain region, calcium indicator, optical configuration, and acquisition parameters). This section explicitly specifies the number of animals, brain region, frame rate, field of view, session duration, and total data volume. We also clarified that conclusions are intended to evaluate MPS performance in this controlled long-duration setting rather than to claim universal parameter generalizability across brain regions, indicators, or optical systems.

(5) Parameter guidance and documentation

Reviewer #2:

...users should not be expected to blindly trust default or suggested parameter selections. Instead, users need guidance on what each modifiable parameter does to their data and how each step analysis output should be interpreted. Currently, the documentation and FAQ website linked to MPS installation does not do an adequate job of describing parameters or their optimization...

We agree that users should not blindly trust default or suggested parameters. We substantially expanded and centralized documentation by adding a parameter-selection walkthrough that explains what each modifiable parameter does, how it affects intermediate and final outputs, and how diagnostic plots generated at each stage should be interpreted. Rather than prescribing dataset-specific parameter values, we explicitly framed parameter selection as an iterative, hypothesis-driven process informed by experimental factors such as calcium indicator kinetics, lens size and numerical aperture, field of view, recording duration, and expected neuronal density. We consolidated previously dispersed explanations from the GitHub repository into a single documentation site and expanded figure descriptions to guide interpretation by less experienced users. A representative sample dataset and accompanying analysis code were made publicly available at https://github.com/ariasarch/MPS_Sample_Code to support parameter exploration on tractable data.

(6) Packaging and distribution

Reviewer #1:

...current best practices in software development increasingly rely on continuous integration and continuous deployment (CI/CD) pipelines to ensure reproducibility, testing, and long-term maintenance. In this context, it has become standard for Python packages to be distributed via PyPI or Conda. Without dismissing the value of standalone installers, the overall quality and sustainability of MPS would be greatly enhanced by also supporting conventional environment-based installations.

Regarding distribution more broadly: while our one-click installers are intended to reduce setup burden for non-programmers, we recognize the value of conventional environment-based distribution for longterm sustainability. We are exploring the feasibility of adding a standard PyPI and/or Conda installation pathway alongside the standalone installers. To ensure reproducibility across environments, all package dependencies are now explicitly version-pinned at installation time, eliminating environment drift as a source of irreproducibility.

We would note, however, that PyPI distribution alone does not fully resolve the reproducibility challenges inherent to scientific Python software. Even with version-pinned dependencies, downstream changes in the Python interpreter itself, compiled extension modules, and platform-specific build toolchains can silently alter numerical behavior in ways that are difficult to anticipate or control. Our standalone installers address this by shipping a complete, fixed execution environment, and we believe this remains a meaningful architectural advantage for ensuring long-term reproducibility - particularly for non-developer users who may not be in a position to diagnose subtle environment-related failures. We see PyPI/Conda support and standalone installers as complementary rather than equivalent approaches, and will pursue both where feasible.

Author response:

The following is the authors’ response to the previous reviews

We appreciate the authors' efforts in addressing the concerns raised, particularly including a variance partitioning approach to analyse their data. Detailed feedback on the revised manuscript are below and we include a brief list of comments that we think the authors could address in the text: 

(1) Justify metric selection - Could you please include in the text and explanation for why only five behavioural metrics were highlighted out of the many you calculated?

We have added explanations throughout the manuscript clarifying the rationale for selecting these behavioral parameters, including in lines 467ff. and 531ff. In short, the five highlighted metrics were chosen because they capture key aspects of the behavioral repertoire and, importantly, can be consistently measured across all experimental conditions. Other parameters were excluded as they were only applicable under specific contexts and thus not suitable for cross-condition comparisons.

(2) Discuss ICC variation - We note that there is variation among the ICC scores for the different metrics you've studied. While this is expected, we ask that you acknowledge in the text that some traits show high repeatability and others low, and reflect this variation in the conclusions.

We have added an additional paragraph in the Discussion (lines 743ff.) addressing the variation in ICC values among behavioral traits. This new section highlights that some metrics show high repeatability while others exhibit lower consistency, and we discuss how this heterogeneity informs our conclusions about individual behavioral stability across contexts.

(3) Tone down general claims - Because of the above point, we recommend that you avoid overstating that individuality persists across all behaviours. Please clarify this in the Abstract and main text that it applies to some traits more than others.

We carefully reviewed the entire manuscript and revised the phrasing wherever necessary to avoid overgeneralization. Statements about individuality have been adjusted to clarify that consistent individuality can be measured in some behavioral traits more strongly than to others, both in the Abstract and throughout the main text.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors state the study's goal clearly: "The goal of our study was to understand to what extent animal individuality is influenced by situational changes in the environment, i.e., how much of an animal's individuality remains after one or more environmental features change." They use visually guided behavioral features to examine the extent of correlation over time and in a variety of contexts. They develop new behavioral instrumentation and software to measure behavior in Buridan's paradigm (and variations thereof), the Y-maze, and a flight simulator. Using these assays, they examine the correlations between conditions for a panel of locomotion parameters. They propose that inter-assay correlations will determine the persistence of locomotion individuality.

Strengths: 

The OED defines individuality as "the sum of the attributes which distinguish a person or thing from others of the same kind," a definition mirrored by other dictionaries and the scientific literature on the topic. The concept of behavioral individuality can be characterized as: (1) a large set of behavioral attributes, (2) with inter-individual variability, that are (3) stable over time. A previous study examined walking parameters in Buridan's paradigm, finding that several parameters were variable between individuals, and that these showed stability over separate days and up to 4 weeks (DOI: 10.1126/science.aaw718). The present study replicates some of those findings, and extends the experiments from temporal stability to examining correlation of locomotion features betweendifferent contexts. 

The major strength of the study is using a range of different behavioral assays to examine the correlations of several different behavior parameters. It shows clearly that the inter-individual variability of some parameters is at least partially preserved between some contexts, and not preserved between others. The development of highthroughput behavior assays and sharing the information on how to make the assays is a commendable contribution.

Weaknesses:

The definition of individuality considers a comprehensive or large set of attributes, but the authors consider only a handful. In Supplemental Fig. S8, the authors show a large correlation matrix of many behavioral parameters, but these are illegible and are only mentioned briefly in Results. Why were five or so parameters selected from the full set? How were these selected? Do the correlation trends hold true across all parameters? For assays in which only a subset of parameters can be directly compared, were all of these included in the analysis, or only a subset?

The correlation analysis is used to establish stability between assays. For temporal retesting, "stability" is certainly the appropriate word, but between contexts it implies that there could be 'instability'. Rather, instead of the 'instability' of a single brain process, a different behavior in a different context could arise from engaging largely (or entirely?) distinct context-dependent internal processes, and have nothing to do with process stability per se. For inter-context similarities, perhaps a better word would be "consistency".

The parameters are considered one-by-one, not in aggregate. This focuses on the stability/consistency of the variability of a single parameter at a time, rather than holistic individuality. It would appear that an appropriate measure of individuality stability (or individuality consistency) that accounts for the high-dimensional nature of individuality would somehow summarize correlations across all parameters. Why was a multivariate approach (e.g. multiple regression/correlation) not used? Treating the data with a multivariate or averaged approach would allow the authors to directly address 'individuality stability', along with the analyses of single-parameter variability stability.

The correlation coefficients are sometimes quite low, though highly significant, and are deemed to indicate stability. For example, in Figure 4C top left, the % of time walked at 23°C and 32°C are correlated by 0.263, which corresponds to an R2 of 0.069 i.e. just 7% of the 32°C variance is predictable by the 23°C variance. Is it fair to say that 7% determination indicates parameter stability? Another example: "Vector strength was the most correlated attention parameter... correlations ranged... to -0.197," which implies that 96% (1 - R2) of Y-maze variance is not predicted by Buridan variance. At what level does an r value not represent stability?

The authors describe a dissociation between inter-group differences and interindividual variation stability, i.e. sometimes large mean differences between contexts, but significant correlation between individual test and retest data. Given that correlation is sensitive to slope, this might be expected to underestimate the variability stability (or consistency). Is there a way to adjust for the group differences before examining correlation? For example, would it be possible to transform the values to ingroup ranks prior to correlation analysis?

What is gained by classifying the five parameters into exploration, attention, and anxiety? To what extent have these classifications been validated, both in general, and with regard to these specific parameters? Is increased walking speed at higher temperature necessarily due to increased 'explorative' nature, or could it be attributed to increased metabolism, dehydration stress, or a heat-pain response? To what extent are these categories subjective?

The legends are quite brief and do not link to descriptions of specific experiments. For example, Figure 4a depicts a graphical overview of the procedure, but I could not find a detailed description of this experiment's protocol.

Using the current single-correlation analysis approach, the aims would benefit from rewording to appropriately address single-parameter variability stability/consistency (as distinct from holistic individuality). Alternatively, the analysis could be adjusted to address the multivariate nature of individuality, so that the claims and the analysis are in concordance with each other.

The study presents a bounty of new technology to study visually guided behaviors. The Github link to the software was not available. To verify successful transfer or openhardware and open-software, a report would demonstrate transfer by collaboration with one or more other laboratories, which the present manuscript does not appear to do. Nevertheless, making the technology available to readers is commendable.

The study discusses a number of interesting, stimulating ideas about inter-individual variability, and presents intriguing data that speaks to those ideas, albeit with the issues outlined above.

While the current work does not present any mechanistic analysis of inter-individual variability, the implementation of high-throughput assays sets up the field to more systematically investigate fly visual behaviors, their variability, and their underlying mechanisms. 

Comments on revisions:

While the incorporation of a hierarchical mixed model (HMM) appears to represent an improvement over their prior single-parameter correlation approach, it's not clear to me that this is a multivariate analysis. They write that "For each trait, we fitted a hierarchical linear mixed-effects model in Matlab (using the fit lme function) with environmental context as a fixed effect and fly identity (ID) as a random intercept... We computed the intraclass correlation coefficient (ICC) from each model as the betweenfly variance divided by total variance. ICC, therefore, quantified repeatability across environmental contexts."

Does this indicate that HMM was used in a univariate approach? Can an analysis of only five metrics of several dozen total metrics be characterized as 'holistic'?

Within Figure 10a, some of the metrics show high ICC scores, but others do not. This suggests that the authors are overstating the overall persistence and/or consistency of behavioral individuality. It is clear from Figure S8 that a large number of metrics were calculated for each fly, but it remains unclear, at least to me, why the five metrics in Figure 10a are justified for selection. One is left wondering how rare or common is the 0.6 repeatability of % time walked among all the other behavioral metrics. It appears that a holistic analysis of this large data set remains impossible. 

We thank the reviewer for the careful and thoughtful assessment of our work.

We have added an additional paragraph in the Discussion (lines 743ff.) explicitly addressing the variation in ICC values among behavioral traits. This section emphasizes that while some metrics show high repeatability, others exhibit lower consistency, and we discuss how this heterogeneity informs our conclusions regarding individual behavioral stability across contexts.

Regarding the reviewer’s concern about the analytical approach, we would like to clarify that the hierarchical linear mixed model (LMM) was applied in a univariate framework—each behavioral metric was analyzed separately to estimate its individual ICC value. This approach allows us to quantify repeatability for each trait across environmental contexts while accounting for individual identity as a random effect. Although this is not a multivariate model in the strict sense, it represents an improvement over the prior pairwise correlation approach because it explicitly partitions within- and between-individual variance.

As for the selection of behavioral metrics, the five parameters highlighted (% time walked, walking speed, vector strength, angular velocity, and centrophobicity) were chosen because they represent key, biologically interpretable dimensions of locomotor and spatial behavior and, importantly, could be measured reliably across all tested conditions. Several other parameters that we routinely analyze (e.g., Linneweber et al., 2020) could not be calculated in all contexts—for instance, under darkness or when visual cues were absent—and therefore were excluded to maintain consistency across assays.

We agree that a truly holistic multivariate comparison across all extracted parameters would be valuable; however, given the contextual limitations of some metrics, such an analysis was not feasible in the present framework. We have clarified these points in the revised manuscript to avoid potential misunderstandings.

The authors write: "...fly individuality persists across different contexts, and individual differences shape behavior across variable environments, thereby making the underlying developmental and functional mechanisms amenable to genetic dissection." However, presumably the various behavioral features (and their variability) are governed by different brain regions, so some metrics (high ICC) would be amenable to the genetic dissection of individuality/variability, while others (low ICC) would not. It would be useful to know which are which, to define which behavioral domains express individuality, and could be targets for genetic analysis, and which do not. At the very least, the Abstract might like to acknowledge that inter-context consistency is not a major property of all or most behavioral metrics.

We thank the reviewer for this helpful comment and agree that not all behavioral traits exhibit the same degree of inter-context consistency. We have clarified this point in the revised Abstract and ensured that it is also reflected in the main text. The Abstract now reads: 

“We find that individuality is highly context-dependent, but even under the most extreme environmental alterations tested, consistency of behavioral individuality always persisted in at least one of the traits. Furthermore, our quantification reveals a hierarchical order of environmental features influencing individuality. We confirmed this hierarchy using a generalized linear model and a hierarchical linear mixed model. In summary, our work demonstrates that, similar to humans, fly individuality persists across different contexts (albeit worse than across time), and individual differences shape behavior across variable environments. The presence of consistency across situations in flies makes the underlying developmental and functional mechanisms amenable to genetic dissection.” 

This revision clarifies that individuality is not uniformly expressed across all behavioral metrics, but rather in a subset of traits with higher repeatability, which are the most promising targets for future genetic analyses.

I hold that inter-trial repeatability should rightly be called "stability" while inter-context repeatability should be called "consistency". In the current manuscript, "consistency" is used throughout the manuscript, except for the new edits, which use "stability". If the authors are going to use both terms, it would be preferable if they could explain precisely how they define and use these terms.

We thank the reviewer for drawing attention to this inconsistency in terminology. We apologize for the oversight and have corrected it throughout the manuscript to ensure uniform usage.

Reviewer #2 (Public review):

Summary:

The authors repeated measured the behavior of individual flies across several environmental situations in custom-made behavioral phenotyping rigs.

Strengths:

The study uses several different behavioral phenotyping devices to quantify individual behavior in a number of different situations and over time. It seems to be a very impressive amount of data. The authors also make all their behavioral phenotyping rig design and tracking software available, which I think is great and I'm sure other folks will be interested in using and adapting to their own needs.

Weaknesses/Limitations: 

I think an important limitation is that while the authors measured the flies under different environmental scenarios (i.e. with different lighting, temperature) they didn't really alter the "context" of the environment. At least within behavioral ecology, context would refer to the potential functionality of the expressed behaviors so for example, an anti-predator context, or a mating context, or foraging. Here, the authors seem to really just be measuring aspects of locomotion under benign (relatively low risk perception) contexts. This is not a flaw of the study, but rather a limitation to how strongly the authors can really say that this demonstrates that individuality is generalized across many different contexts. It's quite possible that rank-order of locomotor (or other) behaviors may shift when the flies are in a mating or risky context. 

I think the authors are missing an opportunity to use much more robust statistical methods. It appears as though the authors used pearson correlations across time/situations to estimate individual variation; however far more sophisticated and elegant methods exist. The problem is that pearson correlation coefficients can be anticonservative and additionally, the authors have thus had to perform many many tests to correlate behaviors across the different trials/scenarios. I don't see any evidence that the authors are controlling for multiple testing which I think would also help. Alternatively, though, the paper would be a lot stronger, and my guess is, much more streamlined if the authors employ hierarchical mixed models to analyse these data, which are the standard analytical tools in the study of individual behavioral variation. In this way, the authors could partition the behavioral variance into its among- and withinindividual components and quantify repeatability of different behaviors across trials/scenarios simultaneously. This would remove the need to estimate 3 different correlations for day 1 & day 2, day 1 & 3, day 2 & 3 (or stripe 0 & stripe 1, etc) and instead just report a single repeatability for e.g. the time spent walking among the different strip patterns (eg. figure 3). Additionally, the authors could then use multivariate models where the response variables are all the behaviors combined and the authors could estimate the among-individual covariance in these behaviors. I see that the authors state they include generalized linear mixed models in their updated MS, but I struggled a bit to understand exactly how these models were fit? What exactly was the response? what exactly were the predictors (I just don't understand what Line404 means "a GLM was trained using the environmental parameters as predictors (0 when the parameter was not change, 1 if it was) and the resulting individual rank differences as the response"). So were different models run for each scenario? for different behaviors? Across scenarios? what exactly? I just harp on this because I'm actually really interested in these data and think that updating these methods can really help clarify the results and make the main messages much clearer!

I appreciate that the authors now included their sample sizes in the main body of text (as opposed to the supplement) but I think that it would still help if the authors included a brief overview of their design at the start of the methods. It is still unclear to me how many rigs each individual fly was run through? Were the same individuals measured in multiple different rigs/scenarios? Or just one?

I really think a variance partitioning modeling framework could certainly improve their statistical inference and likely highlight some other cool patterns as these methods could better estimate stability and covariance in individual intercepts (and potentially slopes) across time and situation. I also genuinely think that this will improve the impact and reach of this paper as they'll be using methods that are standard in the study of individual behavioral variation

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors): 

I am delighted to see the authors have included hierarchical models in their analysis. I really think this strengthens the paper and their conclusions while simultaneously making it more accessible to folks that typically use these types of methods to investigate these patterns of individual behavior. It's also cool, and completely jives with my own experience measuring individual behavior in that the activity metrics show the highest repeatability compared to the more flexible behaviors (such as "exploration"). I think it's quite striking and interesting to see such moderate repeatability estimates in these behaviors across what could be very different environmental scenarios. I think this is a very strong and meaty paper with a lot of information to digest producinghowever a very elegant and convincing take-home message: individuals are unique in their behavior even across very different environments.

We sincerely thank the reviewer for the positive and encouraging feedback, as well as for their valuable input throughout the review process. We are very pleased that the inclusion of hierarchical models and the resulting interpretations resonated with the reviewer’s own experience and perspective.

Reviewer #1 (Public review):

Summary:

The manuscript examines the factors that restrict the induction of IL-17-producing T cells during Mycobacterium tuberculosis (Mtb) infection. The authors show that neither the infectious route nor the duration of infection is responsible. But they do show that mice that lack the Th1-defining transcription factor, a finding consistent with prior reports in the field of immunology. They also show that 2 highly attenuated Mtb mutants in ESX-1 and PDIM, two well-known Mtb virulence factors, do induce IL-17-producing T cells. In contrast, Mtb mutants in mmpl4 are also similarly attenuated, but do not induce IL-17-producing T cells, suggesting that this property is not simply a result of attenuation but due to specific properties of ESX-1 and PDIM-deficient mutants.

Strengths:

(1) It is interesting that mice infected with ESX-1 and PDIM mutants have increased induction of Th17 cells.

(2) The data are solid and convincing throughout.

Weaknesses:

There are two main criticisms:

(1) It is not clear how much the factors uncovered here are true beyond B6 mice. B6 mice, compared to humans, are known to be very Th1-skewed, and Tbet is a strong inhibitor of Th17-specific T cells. Many people make IL-17-producing T cells in response to Mtb infection.

(2) Very few novel insights are mechanistically revealed about how Th17 induction is restricted by Mtb. Tbet induction is known to restrict Th17 development, and this is a T-cell intrinsic mechanism. In contrast, the IL-23 association revealed seems to be extrinsic to T cells and to act on T cells. How, if at all, are these factors related to each other in restricting Th17 induction? Also, the conclusion that it is not a result of attenuation is not completely convincing.

Other points:

(1) The authors show that mice infected with a deficiency in ESX-1 have more IL-17-producing CD4 T cells in response to stimulation with an ESAT-6 peptide pool (Figure 3B). Because ESAT-6 is encoded by ESX-1, why do mice infected with this Mtb mutant have any ESAT-6-specific T cells? Is it an incomplete knockdown?

(2) The manuscript states, "Under the conditions where Th17s are highly induced, mice infected with either ΔESX-1 or PDIM lacking Mtb, the Il17a-/- mice had ~3-5 fold higher CFU than WT mice (Figures 3F-G). These results indicate that the induction of Th17s is not dependent on the attenuation of Mtb in general, but instead Mtb utilizes ESX-1 and PDIM to suppress the induction of a Th17 response that enhances protection against Mtb infection." I don't think the last sentence is necessarily true. I can imagine a scenario in which the induction of the Th17s is, in fact, due to the attenuation, and the Th17 induction still contributes to protection.

(3) ESX-1, PDIM, and mmpl4 mutants all have similarly reduced CFUs in the lung, but what about the LN? The bacterial burden in the LN may be more important for regulating T-bet, IL-23, and Th17 differentiation, since the LN is where T cell priming occurs, than the CFU in the lung. Perhaps ESX-1 and PDIM mutants have reduced CFU in the LN, but mmpl4 does not. This difference in LN burdens may be the primary driver of Th17 priming, as high avidity interactions are thought to be an important driver of T-bet induction.

(4) Do LN cDC1 and high levels of IL-12 p35 in mice infected with the mmpl4 mutant? Likewise, LN cDC2's express low levels of IL-12 p19 (akin to those infected with WT Mtb)? If these observations for ESX-1 and PDIM mutants are mechanistically linked to the increased numbers of Th17 cells, then you would expect mice infected with mmpl4 mutants to be more like those infected with WT Mtb than those infected with ESX-1 and PDIM mutants.

(5) ESX-1 and PDIM are very different virulence factors - a protein secretory pathway and cell wall lipid, respectively? Mechanistically, how would mutants in these pathways give very similar outcomes regarding Th17 cells unless it was simply as an aspect of their attenuation? Perhaps, mmpl4 mutants simply differ in some aspects of their attenuation, such as bacterial burdens in LNs, or their interaction with cDCs?

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors tackle an important question of why IL-17 production and TH17 responses are lower than expected during Mtb infection. The authors identify an axis of cross-regulation between TH1 and TH17 cells and provide data to support roles for Mtb virulence factors ESX1 and PDIM in promoting TH1 responses and/or suppressing TH17 responses.

Strengths:

The strengths include the significance of the work, the combination of host and Mtb genetic models to dissect the mechanistic basis for regulation of IL-17 production from T cells during infection, and the rigor of the experiments. There are a number of exciting findings from the work, including the cross-talk between T cell responses and the impact of ESX1 and PDIM on these responses.

Weaknesses:

The following conclusions and interpretations should be revisited, rephrased, and re-evaluated:

(1) The manuscript neglects to analyze T cell responses in the dLN, which is the critical site where these responses are initiated (only DC cytokine production is measured in the dLN). The differences in the lungs could reflect trafficking of T cells to the lungs, local lung T cell responses, or durability of the T cell responses in the lungs. The authors state in the last results section that "These results indicate that the ESX-1 and PDIM virulence factors impact naïve T cell differentiation at the draining mediastinal lymph node..." but T cell responses are never measured in the dLN.

(2) Figure 2: The authors state that "Importantly, IFN-γ deficient mice did not exhibit elevated levels of IL-17A producing CD4 T cells demonstrating that IFN-γ production is not the mechanism by which Th1 T cells limit a Th17 response during Mtb infection", but the difference is significantly different and even more obvious in Panel B. In fact, if the Panel D y-axis was on a log scale, the Ifng-/- would likely look more like Tbet-/- than WT. Based on this data, it seems like IFNg is having an effect and should not be completely discounted. Does the deletion of Ifng affect the number of Tbet+ T cells?

In addition, the deletion of Tbet results in an increased number of IFNg+IL-17+ double positive T cells (Figure 2B), in addition to a sizable IFNg single positive T cell population maintained in the Tbet-/- mice (10x the negative control of Ifng-/-). Is this why Tbet deletion is not as severe as Ifng deletion, because T cells are still making IFNg?

Along these lines, the statement in the text that, "Tbet-/-Il17a-/- mice completely lacked both IFN-γ producing...." T cells is not supported by the data in Figure 2C. Tbet-/-Il17a-/- mice look to have more gamma-producing T cells than Tbet-/- mice (which is already 10x the negative control of Ifng-/- in panel 2B if one includes the gamma single positive and IFNg/IL-17 double positive).

(3) In the Results sections describing Figures 3, 4, and 5, the authors equate IL-17 production by T cells with TH17 responses and IFNg expression with TH1, but Tbet and RORgt expression in the T cells should be measured to make conclusions about TH1 and TH17. Or the authors can rephrase their findings to specifically state the observations as IFNg or IL-17 expressing CD4+ T cells.

(4) Conceptually, do the authors think that ESX1/PDIM promotes TH1 responses and this blocks TH17 or are ESX1/PDIM blocking TH17 responses directly, allowing for increased TH1 responses? It would be helpful to clarify the model in this regard, describe how the data supports one model or the other, and then make sure the language is consistent throughout. Can these effects on T cell responses be tested and recapitulated in vitro using infected APC and T cell co-cultures?

Reviewer #3 (Public review):

Summary:

The manuscript by Zilinskas et al seeks to understand the mechanisms underlying the ability of Mtb to suppress Th17 differentiation. As Th17 responses are needed for protective immunity against TB, this is an important topic of investigation. They use Mtb mutants that lack eccC1 (from the ESX-1 locus) and fadD28 (encoding PDIM) and implicate a Tbet-dependent pathway by which Mtb modulates Th17 differentiation. The mechanism by which ESX-1/PDIM function to impact Th17 differentiation is, however, unclear, which limits the novelty of the results.

Strengths:

Understanding how Mtb limits Th17 differentiation has implications for vaccine development. Comparative study of KO mice and Mtb mutants is a strength.

Weaknesses:

(1) The authors should acknowledge and reference key findings from the literature that have identified suppression of Th17 differentiation as an Mtb virulence mechanism, e.g., the role of the Hip1 protease and CD40 signaling (Madan-Lala JI 2014, Sia Plos Path 2017, Enriquez iScience 2022) and Khader JI 2005, showing the requirement of IL-23 for Th17 responses in vivo in a TB mouse model.

(2) Addressing several questions related to the Tbet KO mouse experiments would strengthen the study. Do the Tbet KO mice have elevated IL-4/5/13 (which has been previously reported in non-TB studies) in addition to IL-17? The lack of Th17 cells in the IFNg KO compared to the Tbet KO may be due to a difference in timing, since only 3-week data are shown; earlier and later time points would provide better interpretation. The authors do not present any data on neutrophil infiltration in WT vs Tbet KO vs IFNg KO mice. Since IL-17 is known to be important for recruiting neutrophils to the lung, data on neutrophils are important for clarifying the mechanism for the CFU outcomes.

(3) While IL-23 is important for sustaining IL-17 production, IL-6, TGF-b and/or IL-1β are necessary for Th17 polarization. What were the levels of these cytokines in DCs in the lung? (Figure 5). Additionally, Tbet-deficient DCs exhibit impaired activation of antigen-specific Th1 cells and have reduced IL-12 production. Given the data showing higher IL-17 levels in Tbet KO mice, the authors should provide information on the DC phenotype (IL-23, IL-6, etc.) in the Tbet KO experiments.

(4) The mechanism by which ESX-1/PDIM function to impact Th17 differentiation is not clear. While data showing a role for ESX-1 and PDIMs in inhibiting Th17 responses is interesting, there is no insight into the potential mechanism of action. Figure 3 showing reduction in IFNg+ CD4 T cells after infection with eccC1 and fadD28 mutants suggests that this outcome is due to a lower bacterial load relative to WT Mtb at the 3-week time point. Since IFNg is known to suppress IL-17, the higher levels of Th17 cells could be due to the reduction in IFNg due to the attenuated growth of the mutants. Additionally, what was the level of Type I IFNs elicited by these mutants?

(5) Since macrophages have been implicated in the reduced cytokines seen in the ESX-1 mutant, IL-23 and other cytokine data on lung macrophages would complement the DC data.

(6) Figure 5. There are many fewer DCs overall in the eccC1 and fadD28 mutant groups, which could account for the increased % IL-23p19 in DCs (5D). What were the levels of IL-23 in DC1s?

Reviewer #2 (Public review):

Summary:

This paper by Diaz et al. uses the zebrafish model to examine how early embryonic exposure to Chlorpyrifos (CPF), a widely used organophosphate pesticide, induces social behavior deficits later in life. This paper combined behavioral testing, pharmaceutical treatment, genetic manipulation, and multi-omics to test the hypothesis that early CPF increases the abundance of denitrifying bacteria, Pseudomonas, which, in turn, enhances nitric oxide production and induces selective inhibition of HDAC8 and abnormal gene expression in the brain.

Strengths:

(1) The observation that early embryonic CPF exposure causes behavior deficits in juvenile zebrafish is very intriguing. It is especially exciting to see that CPF-induced behavior deficits can be reversed by overnight treatment with butyrate or HDAC1 inhibitors in juvenile zebrafish. In humans, CPF exposure during pregnancy causes brain abnormalities and neurological disorders such as Autism. Though it is far away from the zebrafish experimental study to human application, the experimental effects reported in the paper are still quite thought-provoking.

(2) The authors performed RNA sequencing experiments on control zebrafish, CPF-exposed zebrafish, and CPF-exposed zebrafish that were treated with Butyrate. The data not only showed large-scale transcriptomic changes in the juvenile zebrafish brain in response to embryonic CPF exposure but also showed that many CPF-induced genetic alterations can be alleviated by butyrate exposure later in life.

(3) The authors also performed untargeted metabolomics on zebrafish gut and metagenomic analysis in zebrafish feces samples. The results are interesting and support the conclusion that increased Intestinal Nitric oxide metabolism and the abundance of denitrifying bacteria, such as Pseudomonas, are associated with CPF exposure.

(4) The large datasets presented in the paper will be useful to other researchers interested in understanding how CPF or butyrate alters brain and gut function. It might be useful to generate new hypotheses to power other research lines.

(5) The social preferences, behavior testing, and experimental paradigm used by the paper may also be used by other researchers to investigate the interaction among gene, environmental factors, and brain function.

Weaknesses:

(1) The presented link between gut microbiome and CPF-induced behavior and genetic alteration is an association, but not causation. Although the research data align with the hypothesis, the hypothesis is not fully supported or tested by the data presented in the paper in the current state.

(2) The authors performed several large omic studies. However, some of the presented analyses are relatively simple and incomplete. For example, the authors performed shotgun metagenomic analysis on zebrafish feces. However, the paper only displayed the bacterial taxa differences. Are there any differences in bacterial genetic pathways, especially the pathways associated with microbial nitrogen metabolism? What is the alpha and beta diversity looking like when comparing different experimental groups?

L'Impasse de la Punition à l'École : Vers une Approche Éducative et Restauratrice

Résumé Exécutif

Ce document analyse les limites du système punitif traditionnel en milieu scolaire et explore les alternatives fondées sur la discipline positive et les actions réparatrices.

Le constat central est que la punition, définie historiquement comme le fait de "faire payer", échoue souvent à modifier durablement le comportement des élèves.

Au contraire, elle génère fréquemment des sentiments d'injustice, de rébellion ou de ressentiment (les "4 R").

L'approche proposée repose sur un changement de paradigme : passer d'une culture de la domination à une culture de la coopération, caractérisée par un cadre à la fois ferme et bienveillant.

En se concentrant sur l'acquisition de compétences psychosociales manquantes plutôt que sur le blâme, les établissements peuvent réduire de moitié les taux de récidive, améliorer le climat scolaire et favoriser la réussite académique.

La clé réside dans l'autorégulation de l'adulte et l'implication de l'élève dans la recherche de solutions.

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1. Analyse du Système Punitif Actuel

Définitions et Cadre Légal

Le système éducatif français distingue deux niveaux d'intervention, bien que leurs objectifs finaux (rappeler la règle, stopper un comportement, assurer la sécurité) soient similaires :

| Terme | Champ d'application | Autorité compétente | | --- | --- | --- | | Punition scolaire | Manquements mineurs (retards, manque de travail, bavardages). Outil de proximité. | Enseignant ou personnel éducatif. | | Sanction scolaire | Manquements graves ou répétés, atteintes aux biens ou aux personnes. Inscrite au dossier. | Chef d'établissement ou conseil de discipline. |

L'Échec de la "Logique Interne"

La punition repose sur l'idée que pour inciter un élève à mieux agir, il faut d'abord qu'il se sente mal.

Or, les études et les témoignages cliniques démontrent que la punition déclenche une "logique interne" contre-productive chez l'élève.

Les "4 R" de la punition (selon Jane Nelsen) :

1. Ressentiment : Sentiment d'injustice ("Ce n'est pas juste", "L'adulte ne m'aime pas").

2. Revanche : Volonté de rendre les coups ("Elle a écrasé ma balle, je ne ferai rien dans son cours").

3. Rébellion : Opposition frontale pour prouver son autonomie.

4. Retrait : Soumission apparente cachant une baisse d'estime de soi ou une fuite (malhonnêteté pour ne pas être pris).

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2. Le Changement de Paradigme : De la Domination à la Coopération

Le document souligne que 33 % des enseignants continuent d'utiliser la punition traditionnelle, souvent par manque de temps, de formation ou d'alternatives face à des groupes difficiles.

Le passage à une "action éducative et réparatrice" nécessite de modifier le regard porté sur l'enfant.

La Métaphore de l'Iceberg

Le comportement inapproprié n'est que la partie émergée de l'iceberg. Sous la surface se cachent des émotions, des perceptions et, surtout, des compétences manquantes.

• Approche punitive : Se concentre sur la pointe (le comportement) pour le supprimer par la force.

• Approche éducative : Cherche la compétence manquante (organisation, gestion de la colère, attention) pour l'enseigner.

Les Piliers de l'Alternative

L'alternative ne signifie pas l'absence de cadre, mais l'adoption d'une posture ferme et bienveillante :

• Fermeté : Respect de la règle et de la sécurité du collectif. Le cadre est non négociable.

• Bienveillance : Respect de la dignité de l'élève. On ne porte pas atteinte à son intégrité physique ou morale.

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3. Outils Pratiques pour une Discipline Positive

L'approche se décline en trois axes : prévention, intervention et réparation.

A. La Prévention

• Ritualiser l'autorégulation : Proposer des temps de silence ou de respiration (ex: la "minute d'installation") pour stabiliser le niveau émotionnel de la classe.

• Expliciter le cadre : Co-construire les lignes de conduite avec les élèves pour favoriser leur sentiment d'appartenance et de responsabilité.

• Travailler les contributions : Donner à chaque élève un rôle ou une responsabilité au sein du collectif.

B. L'Intervention (Le Temps de Pause)

Contrairement à l'exclusion-sanction, le temps de pause est un outil de gestion émotionnelle.

• Objectif : Redescendre physiologiquement en zone de calme (sortir du mode "cerveau dans la main" ou réactif).

• Processus : L'élève se rend dans un espace dédié (vie scolaire, bureau calme) non pas pour "réfléchir à ce qu'il a fait" sous la contrainte, mais pour retrouver ses capacités rationnelles.

C. La Réparation (La Recherche de Solution)

La réparation doit être liée, respectueuse, proportionnée et utile.

• Exemple : Un élève oubliant ses affaires ne doit pas simplement copier des lignes, mais identifier trois stratégies concrètes pour ne plus oublier son matériel et en tester une.

• Question clé pour l'adulte : "Quelle compétence a manqué à cet élève et comment puis-je l'aider à l'acquérir ?"

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4. Bénéfices Constatés et Conclusions

Le passage d'un système punitif à un maillage éducatif (incluant la CNV, la justice restaurative ou la discipline positive) produit des résultats tangibles :

1. Diminution de la récidive : Un exemple cité montre une réduction de 50 % des incidents graves en un an après l'adoption d'une démarche restaurative.

2. Amélioration des résultats scolaires : Un élève en sécurité émotionnelle (dans sa "fenêtre de tolérance") est plus apte à l'apprentissage et à la concentration.

3. Restauration du lien : L'approche privilégie le maintien de la relation enseignant-élève, évitant la rupture qui mène souvent à la violence contre l'institution.

4. Apaisement de l'adulte : En sortant de la posture de domination permanente, l'enseignant réduit sa fatigue liée au "faire faire" par la contrainte.

Conclusion synthétique : L'éducation efficace repose sur le principe de Jane Nelsen : "On fait mieux quand on se sent mieux".

La punition traditionnelle, en dégradant l'état émotionnel de l'élève, fait obstacle à l'apprentissage qu'elle prétend pourtant servir.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigate how the anterior claustrum may integrate temporally separated task-relevant signals to guide behavior in a delayed escape paradigm. Because in vivo neural recordings from claustrum during this task are extremely limited - comprising single-trial data with small neuronal samples - the authors adopt a modeling-driven approach. They train recurrent neural networks (RNNs) using only behavioral data (escape latency) to reproduce task performance and then analyze the internal dynamics of the trained networks. Within these networks, they identify a subset of units whose activity exhibits persistent responses and strong correlations with behavior, which the authors label as "claustrum-like." Using dimensionality reduction, decoding, and information-theoretic analyses, they argue that these units dynamically integrate conditioned stimulus (CS) and door-opening signals via nonlinear, trajectory-based population dynamics rather than fixed-point attractor states.

To bridge model predictions and biology, the authors complement the modeling with in vitro slice experiments demonstrating recurrent excitatory connectivity and prolonged activity in the anterior claustrum that depends on glutamatergic transmission. They further compare latent neural trajectories derived from previously published in vivo claustrum recordings to those observed in the RNN, reporting qualitative similarities. Based on these results, the authors propose that the claustrum implements temporal signal integration through recurrent excitatory circuitry and dynamic population trajectories, potentially supporting broader theories of integrative brain function.

Strengths:

This study addresses an important and challenging problem: how to infer population-level computation in a brain structure for which in vivo data are sparse and experimentally constrained. The authors are commendably transparent about these limitations and seek to overcome them through a principled modeling framework. The integration of behavioral modeling, RNN analysis, and slice electrophysiology is ambitious and technically sophisticated.

Several aspects stand out as strengths. First, the behavioral RNN is carefully trained and interrogated using a rich set of modern analytical tools, including cross-temporal decoding, trajectory analysis, and partial information decomposition, providing multiple complementary views of network dynamics. Second, the slice experiments convincingly demonstrate recurrent excitatory connectivity in the anterior claustrum, lending biological plausibility to the model's reliance on recurrent dynamics. Third, the manuscript is clearly written, logically organized, and conceptually engaging, and it offers a coherent mechanistic hypothesis that could guide future large-scale recording experiments.

Importantly, the work has significant heuristic value: rather than merely fitting data, it attempts to generate testable computational ideas about claustral function in a regime where direct empirical access is currently limited.

Weaknesses:

Despite these strengths, the manuscript suffers from a recurring and substantial conceptual issue: systematic over-interpretation of model-data correspondence. While the modeling results are potentially insightful, the extent to which they are presented as recapitulating real claustral neural mechanisms goes beyond what the available data can support.

A fundamental limitation is that the RNN is trained solely on behavioral output, without being constrained by neural data at either single-unit or population levels. As a result, the internal network dynamics are underdetermined and non-unique. Many distinct internal solutions could plausibly generate identical behavior. However, the manuscript frequently treats the specific internal solution discovered in the RNN as if it were a close approximation of the actual claustrum circuit.

This issue is compounded by the sparse nature of the in vivo data used for comparison. The GPFA-based trajectory analyses rely on pseudo-populations and single-trial recordings, yet are interpreted as evidence for robust population-level dynamics. Because neurons were not recorded simultaneously, the inferred trajectories necessarily lack true population covariance and shared trial-to-trial variability, limiting their interpretability as genuine population dynamics. Similarly, conclusions about trajectory-based versus attractor-based computation are drawn almost exclusively from model analyses and then generalized to the biological system.

Overall, while the modeling framework is appropriate as a hypothesis-generating tool, the manuscript repeatedly crosses the line from proposing plausible mechanisms to asserting explanatory or even causal equivalence between the model and the brain. This undermines the otherwise strong contributions of the work.

Below are several specific points that warrant further clarification or revision:

(1) Tone of model-data correspondence

Numerous statements describe the RNN as "closely mimicking," "recapitulating," or being "nearly identical" to claustral neural dynamics, sometimes extending to claims about causal relationships between neural activity and behavior. Given that neural data were not used to train the model, and that only a small subset of trained networks showed the reported dynamics, these statements should be substantially softened throughout the manuscript. The RNN should be framed as providing one possible computational realization consistent with existing data, not as a close instantiation of the biological circuit

(2) Non-uniqueness of RNN solutions

The fact that only a small fraction of trained networks exhibited "claustrum-like" clusters deserves deeper discussion. This observation raises the possibility that the identified solution is fragile or highly specific rather than canonical. The authors should explicitly discuss the non-uniqueness of internal solutions in behavior-trained RNNs, including the range of alternative network dynamics that can reproduce the same behavior. In particular, it should be clarified why the specific network exhibiting "claustrum-like" clusters is informative about claustral computation, rather than representing one arbitrary solution among many.

(3) GPFA trajectory comparisons

The qualitative similarity between RNN trajectories and GPFA-derived trajectories from sparse in vivo data is interesting but insufficient to support claims of robustness or population-level structure. Statements suggesting that these patterns are unlikely to arise from noise or random fluctuations are not justified, given the single-trial, pseudo-population nature of the data. Either additional quantitative controls should be added, or the interpretation should be substantially tempered.

(4) Scope of functional claims

The discussion connecting the findings to broad theories of claustral function, global workspace, or consciousness extends well beyond the data presented. These speculative links should be clearly labeled as such and significantly reduced in strength and prominence.

(5) Comment on Conceptual Interpretation of the Behavioral Paradigm:

The manuscript repeatedly describes the delayed escape task as an "inference-based behavioral paradigm" and states that animals "infer that a value-neutral alternative space is likely to be safer" when the CS is presented in a novel environment. While I appreciate that the US-CS association was established in a different context and that the CS is then presented in a new environment, I am not convinced that the current behavioral evidence uniquely supports an inference interpretation.

First, it is not clear that this task is widely recognized in the literature as a canonical inference task, in the sense of, for example, sensory preconditioning, transitive inference, or model-based inference paradigms. Rather, the observed effect-that CS animals escape faster to a neutral compartment than neutral-CS controls-can be parsimoniously interpreted in terms of generalized threat value, heightened fear/anxiety, or a bias toward avoidance/escape under elevated threat, without requiring an explicit inferential step about the specific safety of the alternative compartment. The fact that no prior training is needed is compatible with flexible generalization, but does not by itself demonstrate inference in a more formal computational sense.

Second, the inference claim becomes central to the manuscript's conceptual framing (e.g., the idea that rsCla supports "inference-based escape"), yet the behavioral analyses presented here and in the cited prior work do not clearly rule out simpler accounts. Clarifying this distinction would help avoid overstating both the inferential nature of the behavior and the specific role of rsCla and the RNN's "claustrum-like" cluster in supporting inference per se, as opposed to more general integration of threat-related signals with an opportunity for escape.

Overall Assessment:

This manuscript presents an interesting and potentially valuable modeling-based framework for thinking about temporal integration in the claustrum, supported by solid slice physiology. However, in its current form, it overstates the degree to which the proposed RNN dynamics reflect actual claustral neural mechanisms. With substantial revision - especially a more cautious interpretation of model-data similarity and a clearer articulation of modeling limitations - the study could make a meaningful contribution as a hypothesis-generating work rather than a definitive mechanistic account.

Reviewer #2 (Public review):

This manuscript reports the behavior of a computational model of rat claustral neurons during the performance of a behavioral task known as the delayed escape task (in this reviewer's understanding, this behavioral task was created and implemented by this group only). These authors have argued in a prior manuscript (Han et al.) that a group of neurons located "rostral to striatum" is part of the claustrum. The group names the region the "rostral to striatum claustrum." Additionally, in the Han et al. paper, the authors argue that these cells are responsible for maintaining a signal that lasts through the delay period.

The main findings of the current paper are:

(1) The authors have built a model network that was trained to show firing similar to what was reported for rats in their prior paper.

(2) The authors' analysis of model behavior is used to suggest that the model network recapitulates biological activity, including the existence of a cluster of cells mainly responsible for the delay period firing.

(3) The authors offer evidence from patch clamp recordings for excitatory interconnections among claustral neurons that are an essential feature of the model network.

A major value of the computational network is that "trials" of the network can be performed. In experiments on animals, only single trials can be used.

Concerns:

(1) This paper is based on behavioral results and neural recordings from their prior paper (Han et al.), but data, e.g., in Figure 1, are not clearly identified as new or as coming from that source. Figure 1A, for example, appears to be taken directly from Han et al. No methods are given in this manuscript for the behavioral testing or the in vivo electrophysiology.

(2) Many other details are unclear. Examples include model training, the weight matrices and how these changed with training (p. 13), equations 2 and 3 (p. 13), the sources for the constants in the equations (p. 14), the methods (anesthesia, stereotaxic coordinates, injection specifics and details for "sparse expression") for the ChrimsonR injections.

(3) The explorations of model behavior are a catalog of everything tried rather than an organized demonstration of what the model can and cannot do. The figures could be reduced in number to emphasize the key comparisons of the different clusters and the model's behavior under different conditions, intended to "test" the model.

(4) On page 6, the E-E connectivity is argued from Shelton et al. (2025) and against Kim et al. (2016), but ignores Orman (2015), which, to this reviewer's knowledge, was the first to demonstrate such connectivity, including the long-duration events and impact of planes of section.

(5) Whereas the authors are entitled to their own opinion of prior work (references 3-8), it is inappropriate to misrepresent prior work as only demonstrating a "limited function" of claustum. Additional papers by Mathur's group and Citri's group are ignored.

In summary, the authors have made a computational model that recapitulates the firing of a subset of potentially claustral neurons during a particular behavioral task (delayed escape is certainly not the only behavior that involves claustrum - see e.g., attention, salience, sleep). If the conclusion is that excitatory claustral cells must be connected to other excitatory claustral cells, such a conclusion is not new, and the electrophysiological E-E metrics are not well quantified (e.g., connectivity frequency, strength of connection). If the model is intended to predict how the claustrum might accomplish any other task, there is insufficient detail to evaluate the model beyond the evidence that the model creates a subset of cells that can sustain firing during the delay period in the delayed escape task.

All relevant work must be appropriately cited throughout the manuscript.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Our goal was to propose a possible computational mechanism underlying information integration in the claustrum, not to claim structural or causal equivalence between the model and the biological circuit. We acknowledge that some expressions in the original manuscript may have been interpreted as exceeding this intention, and we will revise the text to explicitly soften such statements.

It is well established that behavior-trained RNNs can admit multiple internal solutions capable of producing the same behavioral output, and we fully agree with this point. Among the many possible solutions, we focused on networks that exhibited dynamical properties consistent with independently obtained behavioral and physiological findings. Thus, in our view, biological plausibility in this study is not grounded in structural isomorphism, but rather in whether the core population-level dynamical properties observed in the model are reproducible in actual claustral population activity.

We also agree with the reviewer that our original qualitative comparison of GPFA-based latent trajectories did not provide sufficient quantitative support. In the revised manuscript, we have therefore added an eigenvalue-based quantitative analysis of the dimensional structure of population trajectories. This analysis does not depend on the identity of the dimensionality-reduction method itself, but instead focuses on quantifying the geometric structure of population-state trajectories as they evolve over time. Applying the same metric to both the RNN and biological claustrum data revealed consistent condition-specific differences in population dynamics.

This quantitative addition strengthens the previous qualitative trajectory comparison and clarifies that the model implements a specific computational dynamical regime that directionally corresponds to claustral population activity. While this does not imply uniqueness of the model, we believe it suggests that the proposed computational principle represents a biologically realizable candidate mechanism.

(1) Tone of model-data correspondence

Numerous statements describe the RNN as "closely mimicking," "recapitulating," or being "nearly identical" to claustral neural dynamics, sometimes extending to claims about causal relationships between neural activity and behavior. Given that neural data were not used to train the model, and that only a small subset of trained networks showed the reported dynamics, these statements should be substantially softened throughout the manuscript. The RNN should be framed as providing one possible computational realization consistent with existing data, not as a close instantiation of the biological circuit.

We agree with the reviewer’s concern. Expressions such as “closely mimicked,” “nearly identical,” and “recapitulate” will be replaced with more moderate language.

(2) Non-uniqueness of RNN solutions

The fact that only a small fraction of trained networks exhibited "claustrum-like" clusters deserves deeper discussion. This observation raises the possibility that the identified solution is fragile or highly specific rather than canonical. The authors should explicitly discuss the non-uniqueness of internal solutions in behavior-trained RNNs, including the range of alternative network dynamics that can reproduce the same behavior. In particular, it should be clarified why the specific network exhibiting "claustrum-like" clusters is informative about claustral computation, rather than representing one arbitrary solution among many.

As the reviewer noted, behavior-trained RNNs can yield multiple internal solutions that generate the same behavioral output, and we acknowledge this non-uniqueness. However, we do not interpret the relatively low success rate (5/100 networks) as evidence of fragility. Rather, we interpret it as suggesting that the emergence of this particular dynamical regime requires stringent structural constraints.

The computational demands of the task—specifically, the integration of temporally separated signals—drive convergence toward networks capable of sustaining persistent activity through recurrent excitatory connectivity. Indeed, all networks exhibiting a claustrum-like cluster shared a strong recurrent excitatory structure within Cluster 1, a structural feature consistent with our slice electrophysiology findings.

Our criterion for selecting RNNs was their ability to reproduce behavioral and physiological observations from the delayed escape experiment. Excluded RNNs may reflect alternative information-processing strategies characteristic of other brain regions or artificial logical solutions. Importantly, claustrum-like dynamics were not explicitly enforced during training; they emerged spontaneously under behavioral constraints, suggesting that this solution is not arbitrary.

Furthermore, the computational principles derived from the RNN were quantitatively consistent with in vivo single-neuron activity. Using an eigenvalue-based metric (λ₃/Σλ), both the RNN and biological claustrum data showed effects in the same direction. Leave-one-neuron-out analyses further demonstrated that this pattern was broadly distributed across neurons in the claustrum. These convergent results suggest that the identified network captures a computational regime that is consistent with claustral population dynamics, rather than representing an arbitrary solution unrelated to the biological observations.

(3) GPFA trajectory comparisons

The qualitative similarity between RNN trajectories and GPFA-derived trajectories from sparse in vivo data is interesting but insufficient to support claims of robustness or population-level structure. Statements suggesting that these patterns are unlikely to arise from noise or random fluctuations are not justified, given the single-trial, pseudo-population nature of the data. Either additional quantitative controls should be added, or the interpretation should be substantially tempered.

We agree that the original GPFA trajectory comparison in the biological claustrum data remained qualitative and did not sufficiently establish robustness or population-level structure. We have therefore added quantitative analyses in the revised manuscript.

Before presenting these analyses, we clarify methodological limitations inherent in pseudopopulation and single-trial data. GPFA estimates latent trajectories based on covariance structure and temporal smoothness assumptions. In pseudopopulations, true simultaneously recorded covariance cannot be fully reconstructed. Although our dataset is based on single trials rather than trial-to-trial variability, we acknowledge that latent-space estimation depends on covariance structure.

Therefore, the additional quantitative metric is not independent of the GPFA estimation stage; rather, it evaluates the geometric structure of single-trial latent trajectories estimated by GPFA.

Specifically, for biological data, we reanalyzed GPFA-estimated latent trajectories in PCA space and computed an eigenvalue-based metric (λ₃/Σλ). Across 20 time bins, a sliding window of 10 bins was applied. For each window, we computed the covariance matrix and extracted eigenvalues for PC1, PC2, and PC3. The third eigenvalue (λ₃) was normalized by total variance (Σλ = λ₁ + λ₂ + λ₃). This metric quantifies the extent to which trajectories deviate from a planar (two-dimensional) structure into a third dimension. An increase in λ₃/Σλ indicates the formation of a higher-dimensional geometric structure.

For RNN data, since all unit activities were simultaneously observed and sufficient trials were available, we directly applied PCA to population activity without GPFA. Mean trajectories across trials were computed, and the same λ₃/Σλ metric was applied. Although the initial dimensionality-reduction steps differ, the final metric definition and computation are identical. Thus, the comparison focuses on geometric dimensional structure rather than the dimensionality-reduction method itself.

Importantly, within the biological dataset, GPFA estimation, preprocessing, pseudopopulation construction, subsampling strategy, temporal alignment, and smoothing were applied identically across the CS and Neutral conditions. Under this common analysis framework, λ₃/Σλ values were consistently higher in the CS condition than in the Neutral condition.

For the RNN data, an identical analysis pipeline was applied across the CS+Open and Open-only conditions. In this case as well, λ₃/Σλ values were significantly higher in the CS+Open condition than in the Open-only condition.

If structural bias arose from covariance estimation or dimensionality reduction, it would be expected to affect conditions similarly within each dataset. The observation that λ₃/Σλ increases selectively in the CS condition in biological data and in the CS+Open condition in the RNN therefore supports the interpretation that the effect reflects a condition-specific dynamical difference rather than an artifact of dimensionality reduction.

To further examine whether the effect was driven by a small subset of neurons, we performed leave-one-neuron-out analyses in the biological dataset. In the CS group, most neurons contributed relatively evenly to the metric, whereas such distributed contribution was not observed in the Neutral group. This suggests that the three-dimensional structure reflects an organized population-level phenomenon rather than covariance dominated by a small number of outlier neurons.

These results indicate that the consistent elevation of λ₃/Σλ in the CS condition (biological data) and in the CS+Open condition (RNN) reflects a genuine dynamical feature rather than an artifact arising from pseudopopulation construction or dimensionality reduction.

Taken together, the three-dimensional geometric structure observed in GPFA-based latent trajectories is unlikely to reflect random noise. The replication of the same quantitative metric in the RNN, using an independent dimensionality-reduction procedure, strengthens the correspondence between the two systems. We appreciate the reviewer’s suggestion for quantitative reinforcement, which has substantially strengthened the manuscript.

(4) Scope of functional claims

The discussion connecting the findings to broad theories of claustral function, global workspace, or consciousness extends well beyond the data presented. These speculative links should be clearly labeled as such and significantly reduced in strength and prominence.

We agree with the reviewer and will clearly indicate that references to broader theoretical interpretations are speculative. We will substantially reduce their strength and emphasis.

(5) Comment on Conceptual Interpretation of the Behavioral Paradigm:

The manuscript repeatedly describes the delayed escape task as an "inference-based behavioral paradigm" and states that animals "infer that a value-neutral alternative space is likely to be safer" when the CS is presented in a novel environment. While I appreciate that the US-CS association was established in a different context and that the CS is then presented in a new environment, I am not convinced that the current behavioral evidence uniquely supports an inference interpretation.

We agree with the reviewer’s concern. We will describe the delayed escape task as “a behavioral paradigm that requires integration of temporally separated task-relevant signals” and remove inference-related terminology throughout the manuscript.

Reviewer #2 (Public review):

We appreciate the reviewer’s constructive and well-balanced comments. We regret that some of our wording and the scope of our introduction and discussion may not have appropriately reflected the contributions of prior studies. We will revise the manuscript accordingly to ensure that previous literature is more accurately and fairly acknowledged. In addition, we will reorganize the figures to more clearly present the hypotheses being tested and will provide additional details regarding both the modeling framework and the experimental procedures.

(1) This paper is based on behavioral results and neural recordings from their prior paper (Han et al.), but data, e.g., in Figure 1, are not clearly identified as new or as coming from that source. Figure 1A, for example, appears to be taken directly from Han et al. No methods are given in this manuscript for the behavioral testing or the in vivo electrophysiology.

We will clarify more explicitly which data and methods originate from Han et al. (2024). In the original manuscript, Figure 1 panels A, D, E, F, and L (left) were indicated in the legend as originating from Han et al. (2024). We will further clarify this distinction in the main text. Additionally, we will briefly describe the behavioral experiments and in vivo electrophysiology performed in Han et al. in the Methods section, with appropriate citation.

(2) Many other details are unclear. Examples include model training, the weight matrices and how these changed with training (p. 13), equations 2 and 3 (p. 13), the sources for the constants in the equations (p. 14), the methods (anesthesia, stereotaxic coordinates, injection specifics and details for "sparse expression") for the ChrimsonR injections.

As requested, we will provide additional details regarding model training procedures, weight matrices and their evolution during training, equations (2) and (3), the origin of constants used in the equations, and detailed methods for ChrimsonR injection (anesthesia, stereotaxic coordinates, injection parameters, and clarification of “sparse expression”).

(3) The explorations of model behavior are a catalog of everything tried rather than an organized demonstration of what the model can and cannot do. The figures could be reduced in number to emphasize the key comparisons of the different clusters and the model's behavior under different conditions, intended to "test" the model.

We will reorganize the figures to emphasize core results and clarify that the primary goal is to test and validate the computational model.

(4) On page 6, the E-E connectivity is argued from Shelton et al. (2025) and against Kim et al. (2016), but ignores Orman (2015), which, to this reviewer's knowledge, was the first to demonstrate such connectivity, including the long-duration events and impact of planes of section.

We will cite Orman (2015) as suggested and note that persistent activity has been observed in slices cut at specific angles, consistent with our findings.

(5) Whereas the authors are entitled to their own opinion of prior work (references 3-8), it is inappropriate to misrepresent prior work as only demonstrating a "limited function" of claustum. Additional papers by Mathur's group and Citri's group are ignored.

We will remove wording implying “limited” prior work and appropriately acknowledge contributions from the Mathur and Citri groups.

In summary, the authors have made a computational model that recapitulates the firing of a subset of potentially claustral neurons during a particular behavioral task (delayed escape is certainly not the only behavior that involves claustrum - see e.g., attention, salience, sleep). If the conclusion is that excitatory claustral cells must be connected to other excitatory claustral cells, such a conclusion is not new, and the electrophysiological E-E metrics are not well quantified (e.g., connectivity frequency, strength of connection). If the model is intended to predict how the claustrum might accomplish any other task, there is insufficient detail to evaluate the model beyond the evidence that the model creates a subset of cells that can sustain firing during the delay period in the delayed escape task.

Across all whole-cell recordings, optogenetic responses were observed in 38 out of 43 patched cells (~90%), suggesting that a high proportion of claustral neurons receive intra-claustral excitatory input. However, precise connectivity frequency and strength cannot be determined from the current dataset.

As the reviewer noted, our RNN is specialized for the delayed escape task, and we do not claim direct generalization to other proposed claustral functions such as attention, salience, or sleep. The goal of this study is to computationally characterize the temporal integration mechanism observed in this specific task.

While our model is specific to the delayed escape task, the computational principle identified here—nonlinear trajectory-based temporal integration supported by recurrent excitatory connectivity—may represent a more general mechanism for integrating temporally separated signals. However, testing such generality lies beyond the scope of the present study and will be framed as a future direction in the revised Discussion.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The electrocardiogram (ECG) is routinely used to diagnose and assess cardiovascular risk. However, its interpretation can be complicated by sex-based and anatomical variations in heart and torso structure. To quantify these relationships, Dr. Smith and colleagues developed computational tools to automatically reconstruct 3D heart and torso anatomies from UK Biobank data. Their regression analysis identified key sex differences in anatomical parameters and their associations with ECG features, particularly post-myocardial infarction (MI). This work provides valuable quantitative insights into how sex and anatomy influence ECG metrics, potentially improving future ECG interpretation protocols by accounting for these factors.

Strengths:

(1) The study introduces an automated pipeline to reconstruct heart and torso anatomies from a large cohort (1,476 subjects, including healthy and post-MI individuals).

(2) The 3-stage reconstruction achieved high accuracy (validated via Dice coefficient and error distances).

(3) Extracted anatomical features enabled novel analyses of disease-dependent relationships between sex, anatomy, and ECG metrics.

(4) Open-source code for the pipeline and analyses enhances reproducibility.

Weaknesses:

(1) The linear regression approach, while useful, may not fully address collinearity among parameters (e.g., cardiac size, torso volume, heart position). Although left ventricular mass or cavity volume was selected to mitigate collinearity, other parameters (e.g., heart center coordinates) could still introduce bias.

(2) The study attributes residual ECG differences to sex/MI status after controlling for anatomical variables. However, regression model errors could distort these estimates. A rigorous evaluation of potential deviations (e.g., variance inflation factors or alternative methods like ridge regression) would strengthen the conclusions.

(3) The manuscript's highly quantitative presentation may hinder readability. Simplifying technical descriptions and improving figure clarity (e.g., separating superimposed bar plots in Figures 2-4) would aid comprehension.

(4) Given established sex differences in QTc intervals, applying the same analytical framework to explore QTc's dependence on sex and anatomy could have provided additional clinically relevant insights.

We thank Reviewer 1 for their kind and constructive comments. While we have thoroughly addressed all specific recommendations below, in brief, we have added new analysis of the variance inflation factor in Supplementary Tables 2 and 3 to reassure readers that the chosen parameter sets exhibit low levels of collinearity, and provided more explanation for why the relative positional parameters were chosen to avoid this issue. We have added explanatory figures for all positional and orientational parameters to improve understanding of the technical details, and improved clarity of existing figures as detailed below. We welcome the suggestion to add QT interval to the manuscript – whilst this was only available in the UK Biobank for a single lead, we have included an analysis of both QT and QTc intervals in this lead to Page 10, and added some discussion of this to the second full paragraph of Page 14.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comment 1: “Collinearity and Regression Analysis: It would be valuable to assess the collinearity among the regressed parameters (e.g., cardiac size, torso volume, heart center positions [x, y, z], and cardiac orientation angles) and evaluate whether alternative regression methods (e.g., ridge regression) might improve robustness. Additionally, cardiac digital twinning with electrophysiological models could help isolate the exact contribution of electrophysiology while enabling sensitivity analysis. Nonlinear regression or machine learning approaches might also enhance the predictive power of the analysis.”

We thank the reviewer for drawing attention to the important issue of collinearity in the parameter sets used in the regression analysis. To address this, we have added Supplementary Tables 2 and 3, which detail the variance inflation factors for each of the parameter sets used. This was considered in the selection of anatomical parameters – e.g. using relative position not absolute distances between landmarks, which would be more collinear. As these are all below a value of 3.4, we believe that the effect of collinearity is limited, and thus to reduce subjectivity of parameter selection in more complex methods, and encourage interpretability, we have retained our linear regression analysis. In addition, we have added an explanation to the second full paragraph on Page 6 of how we calculated the relative, rather than absolute position of the cardiac centre partially to avoid the problem of collinearity when using multiple absolute distances. We concur that modelling and simulation techniques are well suited to explore the electrophysiological component further – as this is out of the scope of this work, we have addressed the role of these methods in future work in the final paragraph of Page 16.

Comment 2: “Figure Clarity (Bar Plots): The superimposed bar plots in Figures 2-4 are difficult to interpret; separating the bars for each coefficient would improve readability.”

We accept that the stacked bar plots could be improved in their clarity. Whilst plotting each anatomical parameter separately multiplies the number of plots by a factor of nine, and makes comparison between parameters more difficult, we have added clear horizontal grid lines in order to make values easier to read and interpret.

Comment 3: “Feature Extraction Visualization: A schematic figure illustrating the steps for measuring heart positional parameters (e.g., with example annotations) would help readers better understand the feature extraction methodology.”

We agree with the reviewer that the calculation of positional and orientational parameters is crucial to illustrate clearly. We have included additional Supplementary Figures 2 and 3 to better convey these parameters.

Reviewer #2 (Public review):

Summary:

Missed diagnosis of myocardial ischemia (MI) is more common in women, and treatment is typically less aggressive. This diagnosis stems from the fact that women's ECGs commonly exhibit 12 lead ECG biomarkers that are less likely to fall within the traditional diagnostic criteria. Namely, women have shorter QRS durations and lower ST junction and T wave amplitudes, but longer QT intervals, than men. To study the impact, this study aims to quantify sex differences in heart-torso anatomy and ECG biomarkers, as well as their relative associations, in both pre- and post-MI populations. A novel computational pipeline was constructed to generate torso-ventricular geometries from cardiac magnetic resonance imaging. The pipeline was used to build models for 425 post-myocardial infarction subjects and 1051 healthy controls from UK Biobank clinical images to generate the population.

Strengths:

This study has a strength in that it utilizes a large patient population from the UK Biobank (425 postMI and 1051 healthy controls) to analyze sex-based differences. The computational pipeline is stateof-the-art for constructing torso-ventricular geometries from cardiac MR and is clinically viable. It draws on novel machine learning techniques for segmentation, contour extraction, and shape modeling. This pipeline is publicly available and can help in the large-scale generation of anatomies for other studies. This allows computation of various anatomical factors (torso volume, cavity volume, etc), and subsequent regression analysis on how these factors are altered before and after MI from the 12-lead ECG.

Weaknesses:

Major weaknesses stem from the fact that, while electrophysiological factors appear to play a role across many leads, both post-MI and healthy, the electrophysiological factors are not stated or discussed. The computational modeling pipeline is validated for reconstructing torso contours; however, potential registration errors stemming from ventricular-torso construction are not addressed within the context of anatomical factors, such as the tilt and rotation of the heart. This should be discussed as the paper's claims are based on these results. Further analysis and explanation are needed to understand how these sex-specific results impact the ECG-based diagnosis of MI in men and women, as stated as the primary reason for the study at the beginning of the paper. This would provide a broader impact within the clinical community. Claims about demographics do not appear to be supported within the main manuscript but are provided in the supplements. Reformatting the paper's structure is required to efficiently and effectively present and support the findings and outcomes of this work.

We thank Reviewer 2 for their considered and detailed feedback. We greatly appreciate the invitation to elaborate on the electrophysiological factors, and we have added discussion of this matter to the second and third full paragraphs on Page 14, extending to Page 15 and first full paragraph on Page 15, and highlighted the role of modelling and simulation in future work on the third full paragraph of Page 16. We agree that registration errors are one reason behind remaining reconstruction errors and feel a strength of our study is that the large number of subjects used aided in reducing the effect of this noise, and have updated the second full paragraph of Page 16 to reflect this. We are wary of moving too many supplemental figures and tables describing demographic trends to the main manuscript for fear of diluting the specific answers to our research questions. We have however actioned the suggestions as detailed below to reformat the paper, including redressing the balance of supplemental versus main methodological sections, and thank the reviewer for their guidance in increasing our clarity.

Reviewer #2 (Recommendations for the authors):

(1) Please detail what "chosen to be representative of the underlying dataset" means in terms of a validation dataset.

We thank the reviewer for addressing the lack of clarity in this matter. We have added a reference in the third full paragraph on Page 6 to Supplementary Appendix 1.1, where we have included full details of the selection criteria.

(2) “Current guidelines ... further research [16]." The paragraph should begin with a broader statement that is relevant to the fact that the entire body of work focuses on ECG-based diagnosis differences in women, rather than LVEF through echocardiography.

We have revised the introduction to Paragraph 3 on Page 3 to clarify our motivation for focusing on the ECG in order to shape proposals for novel ECG-based risk stratification tools.

(3) The last paragraph of the introduction should more clearly state what was performed and how you aim to prove your hypothesis. There is no mention of the data, the regression model, or other key aspects important to the reader.

We have added methodological details to Paragraph 5 on Page 3 in order to clarify our approach in testing our hypothesis.

(4) An overview paragraph should be included in the Methods at the beginning.

We thank the reviewer for this valuable suggestion – we have added an overview paragraph to the start of the methodology section on Page 5.

(5) The computational pipeline portion of the methods should be written in full paragraphs instead of almost a bulleted list. In general, more details from the supplement should be provided in the methods.

We thank the reviewer for raising important points concerning the balance of methodological description in the main manuscript and the supplementary materials. We have added detailed description of the reconstruction pipeline to Pages 5 and 6. We feel that the ordered format of the methods section adds to the reproducibility and transparency of our methodology.

(6) The torso reconstruction method was already validated in Smith et al. [29]. What value does your additional validation bring to this methodology? Furthermore, how does the construction of the ventricular-torso reconstructions using the cardiac axes (not just the torso contours) influence ECG metrics?

We apologise that this was not clear – we have clarified in Paragraph 4 on Page 5 that while Smith et al. 2022 provided a detailed validation to the contour extraction networks, it did not validate the torso reconstruction pipeline, as it only presents the reconstruction of two cases as a proof of concept. We have also expanded the second full paragraph on Page 6 to explain that the sparse (but not dense) cardiac anatomies were constructed in order to calculate the cardiac size, which we found was a key factor moderating many ECG biomarkers. We also specified that the cardiac position and orientation were necessary in order to relate these to the torso axes and positions of the ECG electrodes.

(7) Include the details of the regression analysis in the main body of the methods for the readers. This is crucial to the claims and outcomes of the paper. Only a sentence is included in the results and one in the figure: "Each factor's contribution is calculated from the product of the regression coefficients and anatomical sex differences (Supplementary Appendix 1.5)." What specific contributions can I expect to see in the results figures? The results are filled with methodological aspects that should be in the results.

We thank the reviewer again for this important comment regarding the balance of the main text methodology and supplementary methodology sections. We have added detail to the statistical analysis section of the main text on Pages 7 and 8 in order for the reader to understand the following results section without consulting the supplemental methods. We have also removed these details from the results section.

(8) What is "the remaining estimated effect of electrophysiology". Did you do simulations on the electrophysiology, or how is this computed from the clinical data of patients? More explanation is needed, as without this, the paper is just focusing on anatomy.

We have clarified this important point by moving the explanation of the methodology underpinning our estimation of the electrophysiological contributions using the clinical ECGs from the supplementary methods to the main manuscript on the second full paragraph on Page 7, and continuing to Page 8. We have also specified the role of simulations studies in future work on the final paragraph on Page 16.

(9) Include an overview paragraph of the methods to create more structure.

We thank the reviewer again for the further attention to this issue – as previously, we have added an overview paragraph to the methodology section on Page 5.

(10) Only 19.8% of the patients were female, which is probably due to females having a more severe presentation of the disease. How does this impact, bias, or skew your results?

This comment raises a very interesting point, and while the origin of this imbalance is of course multifactorial – women likely do have lower rates of MI events due to the cardioprotective role of estrogen and different health promoting behaviours, and our sex imbalance was reflective of wider trends in MI diagnosis. However, as mentioned in Paragraph 2 Page 3 of the text, there are more missed MI diagnoses in women, and we agree that this may lead to a more severe presentation of female MI pathophysiology. We have expanded the first full paragraph on Page 16 to specify the ECG and demographic impacts that this has on our results, and that it is a strength of this work that we may contribute to future adjustment of the diagnostic criteria, such that future investigations do not have this bias, and that clinical outcomes are improved.

(11) A lot of extra information is provided in Tables 1 and 2. Include additional information in the supplements that is not directly relevant to your findings.

We agree that Table 2 is supplementary, rather than critical information, and have moved it accordingly to the Supplementary Materials on Page 38. We do believe that Table 1 is central for understanding the extracted dataset.

(12) Combine paragraphs 3 and 4 into a single paragraph. "Current guidelines..." and "T wave amplitude...". They are part of a single coherent concept.

We have removed the paragraph break on Page 3 Paragraph 3.

(13) Check all acronyms throughout the paper. The abbreviation for sudden cardiac death (SCD) is only used once in the same paragraph. Remove the acronym and type it out. T-wave amplitude (TWA) is introduced twice in a Figure caption and not introduced until the methods.

Many thanks for this suggestion – we have reviewed all acronyms in the manuscript.

(14) "Figure 1B showcases the capability of the computational pipeline to extract torso contours and reconstruct them into 3D meshes". Isn't this Figure 1A?

We apologise that this was unclear, and have updated the sentence on the first full paragraph of Page 8 to clarify the purpose of Figure 1B.

(15) No need to state: "Female y-axis limits have been adjusted by the difference in healthy QRS duration between sexes for ease of comparison" in the Figure 2 caption.

We have removed this statement on all relevant captions.

(16) The paragraph "For lead V6, 15.9% of healthy subjects..." can be combined with the previous section.

We have removed this paragraph break on Page 9 to improve readability.

(17) The only demographics I could find were age and BMI. State which demographics you used explicitly. This is especially true when the discussion makes claims like "Our findings suggest that corrected QRS duration taking into consideration demographics...". How did you take them into account?

We accept that our previous description of the demographic adjustment to QRS duration in the discussion did not adequately reflect the comprehensiveness of our approach, and have adjusted the second paragraph on Page 14 to rectify this.

(18) The results section is also almost a bulleted list that should be written and reformatted into paragraphs.

The ordered style of our results section was designed to compare how our obtained data answers our research question differently for ECG intervals, amplitudes, and axis angles. Whilst we have adjusted paragraph breaks and moved methodological details to more appropriate sections, we have retained this stylistic choice.

(19) The following sentence should be in the introduction: "Alterations to the polarity and amplitude of the T wave are used in the diagnosis of acute MI [42] and TWA affects proposed risk stratification tools, particularly markers of repolarization abnormalities [9, 43]."

We thank the reviewer for this suggestion. We have included the discussion of how TWA is separately used in proposed risk stratification and current diagnostic tools in Paragraph 3 of Page 3.

Reviewer #1 (Public review):

Summary:

The electrocardiogram (ECG) is routinely used to diagnose and assess cardiovascular risk. However, its interpretation can be complicated by sex-based and anatomical variations in heart and torso structure. To quantify these relationships, Dr. Smith and colleagues developed computational tools to automatically reconstruct 3D heart and torso anatomies from UK Biobank data. Their regression analysis identified key sex differences in anatomical parameters and their associations with ECG features, particularly post-myocardial infarction (MI). This work provides valuable quantitative insights into how sex and anatomy influence ECG metrics, potentially improving future ECG interpretation protocols by accounting for these factors.

Strengths:

(1) The study introduces an automated pipeline to reconstruct heart and torso anatomies from a large cohort (1,476 subjects, including healthy and post-MI individuals).

(2) The 3-stage reconstruction achieved high accuracy (validated via Dice coefficient and error distances).

(3) Extracted anatomical features enabled novel analyses of disease-dependent relationships between sex, anatomy, and ECG metrics.

(4) Open-source code for the pipeline and analyses enhances reproducibility.

Weaknesses:

(1) The linear regression approach, while useful, may not fully address collinearity among parameters (e.g., cardiac size, torso volume, heart position). Although left ventricular mass or cavity volume was selected to mitigate collinearity, other parameters (e.g., heart center coordinates) could still introduce bias.

(2) The study attributes residual ECG differences to sex/MI status after controlling for anatomical variables. However, regression model errors could distort these estimates. A rigorous evaluation of potential deviations (e.g., variance inflation factors or alternative methods like ridge regression) would strengthen the conclusions.

(3) The manuscript's highly quantitative presentation may hinder readability. Simplifying technical descriptions and improving figure clarity (e.g., separating superimposed bar plots in Figures 2-4) would aid comprehension.

(4) Given established sex differences in QTc intervals, applying the same analytical framework to explore QTc's dependence on sex and anatomy could have provided additional clinically relevant insights.

Reviewer #1 (Public review):

Summary:

In this study, the authors trained rats on a "figure 8" go/no-go odor discrimination task. Six odor cues (3 rewarded and 3 non-rewarded) were presented in a fixed temporal order and arranged into two alternating sequences that partially overlap (Sequence #1: 5⁺-0^--1^--2⁺; Sequence #2: 3⁺-0^--1^--4⁺) --forming an abstract figure-8 structure of looping odor cues.

This task is particularly well-suited for probing representations of hidden states, defined here as the animal's position within the task structure beyond superficial sensory features. Although the task can be solved without explicit sequence tracking, it affords the opportunity to generalize across functionally equivalent trials (or "positions") in different sequences, allowing the authors to examine how OFC representations collapse across latent task structure.

Rats were first trained to criterion on the task and then underwent 15 days of self-administration of either intravenous cocaine (3 h/day) or sucrose. Following self-administration, electrodes were implanted in lateral OFC, and single-unit activity was recorded while rats performed the figure-8 task.

Across a series of complementary analyses, the authors report several notable findings. In control animals, lOFC neurons exhibit representational compression across corresponding positions in the two sequences. This compression is observed not only in trial/positions involving overlapping odor (e.g., Position 3 = odor 1 in sequence 1 vs sequence 2), but also in trials/positions involving distinct, sequence-specific odors (e.g., Position 4: odor 2 vs odor 4) --indicating generalization across functionally equivalent task states. Ensemble decoding confirms that sequence identity is weakly decodable at these positions, consistent with the idea that OFC representations collapse incidental differences in sensory information into a common latent or hidden state representation. In contrast, cocaine-experienced rats show persistently stronger differentiation between sequences, including at overlapping odor positions.

Strengths:

- Elegant behavioral design that affords the detection of hidden-state representations.<br /> - Sophisticated and complementary analytical approaches (single-unit activity, population decoding, and tensor component analysis).

Weaknesses:

-The number of subjects is small --can't fully rule out idiosyncratic, animal-specific effects.

Comments on revisions:

The authors have thoroughly addressed all of my previous comments. Congratulations on an excellent paper!

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this study, the authors trained rats on a "figure 8" go/no-go odor discrimination task. Six odor cues (3 rewarded and 3 non-rewarded) were presented in a fixed temporal order and arranged into two alternating sequences that partially overlap (Sequence #1: 5⁺-0^--1^--2⁺; Sequence #2: 3⁺-0^--1^--4⁺) - forming an abstract figure-8 structure of looping odor cues.

This task is particularly well-suited for probing representations of hidden states, defined here as the animal's position within the task structure beyond superficial sensory features. Although the task can be solved without explicit sequence tracking, it affords the opportunity to generalize across functionally equivalent trials (or "positions") in different sequences, allowing the authors to examine how OFC representations collapse across latent task structure.

Rats were first trained to criterion on the task and then underwent 15 days of self-administration of either intravenous cocaine (3 h/day) or sucrose. Following self-administration, electrodes were implanted in lateral OFC, and single-unit activity was recorded while rats performed the figure-8 task.

Across a series of complementary analyses, the authors report several notable findings. In control animals, lOFC neurons exhibit representational compression across corresponding positions in the two sequences. This compression is observed not only in trial/positions involving overlapping odor (e.g., Position 3 = odor 1 in sequence 1 vs sequence 2), but also in trials/positions involving distinct, sequence-specific odors (e.g., Position 4: odor 2 vs odor 4) - indicating generalization across functionally equivalent task states. Ensemble decoding confirms that sequence identity is weakly decodable at these positions, consistent with the idea that OFC representations collapse incidental differences in sensory information into a common latent or hidden state representation. In contrast, cocaine-experienced rats show persistently stronger differentiation between sequences, including at overlapping odor positions.

Strengths:

Elegant behavioral design that affords the detection of hidden-state representations.

Sophisticated and complementary analytical approaches (single-unit activity, population decoding, and tensor component analysis).

Weaknesses:

The number of subjects is small - can't fully rule out idiosyncratic, animal-specific effects.

Comments

(1) Emergence of sequence-dependent OFC representations across learning.

A conceptual point that would benefit from further discussion concerns the emergence of sequence-dependent OFC activity at overlapping positions (e.g., position P3, odor 1). This implies knowledge of the broader task structure. Such representations are presumably absent early in learning, before rats have learned the sequence structure. While recordings were conducted only after rats were well trained, it would be informative if the authors could comment on how they envision these representations developing over learning. For example, does sequence differentiation initially emerge as animals learn the overall task structure, followed by progressive compression once animals learn that certain states are functionally equivalent? Clarifying this learning-stage interpretation would strengthen the theoretical framing of the results.

We agree that the emergence of sequence-dependent OFC activity at overlapping positions (e.g., P3) implies knowledge of the broader task structure and therefore must depend on learning. Although we did not record during early acquisition in the current study, we can outline a learning-stage framework consistent with both prior work and the comparative analyses included here and include it in the discussion.

We think the development of OFC representations is a multi-stage process. Early in learning, before animals have acquired the sequential structure of the task, OFC activity is likely dominated by local sensory features and immediate reinforcement history, with little differentiation between sequences at overlapping positions. As animals learn that odors are embedded within extended sequences that have utility for predicting future outcomes, OFC representations would begin to differentiate identical sensory cues based on their sequence context, giving rise to sequence-dependent activity at positions such as P3. This stage reflects acquisition of the broader task structure and the recognition that current cues carry information about future states.

With continued training, however, OFC representations normally undergo a further refinement: positions that differ in sensory identity but are functionally equivalent become compressed, while distinctions that are irrelevant for guiding behavior are suppressed. Evidence for this later stage comes from our over-trained control animals, in which discrimination between overlapping positions is near chance across most trial epochs, and from prior work using the same task in less-trained animals, where sequence-dependent discrimination is more strongly preserved. Thus, sequence differentiation appears to emerge during structure learning but is subsequently down weighted as animals learn which distinctions are behaviorally irrelevant.

Within this framework, prior cocaine exposure appears to interfere specifically with this later refinement stage. Cocaine-experienced rats exhibit OFC representations resembling those seen earlier in learning—retaining sequence-dependent discrimination at overlapping and functionally equivalent positions—despite extensive training. This suggests not a failure to acquire task structure per se, but rather an impairment in the ability to collapse across states that share common underlying causes.

(2) Reference to the 24-odor position task

The reference to the previously published 24-odor position task is not well integrated into the current manuscript. Given that this task has already been published and is not central to the main analyses presented here, the authors may wish to a) better motivate its relevance to the current study or b) consider removing this supplemental figure entirely to maintain focus.

Thanks for your suggestion, we have removed this supplemental figure as suggested.

(3) Missing behavioral comparison

Line 117: the authors state that absolute differences between sequences differ between cocaine and sucrose groups across all three behavioral measures. However, Figure 1 includes only two corresponding comparisons (Fig. 1I-J). Please add the third measure (% correct) to Figure 1, and arrange these panels in an order consistent with Figure 1F-H (% correct, reaction time, poke latency).

Thanks for your suggestion, we have included the related figure as suggested.

(4) Description of the TCA component

Line 220: authors wrote that the first TCA component exhibits low amplitude at positions P1 and P4 and high amplitude at positions P2 and P3. However, Figure 3 appears to show the opposite pattern (higher magnitude at P1 and P4 and lower magnitude at P2 and P3). Please check and clarify this apparent discrepancy. Alternatively, a clearer explanation of how to interpret the temporal dynamics and scaling of this component in the figure would help readers correctly understand the result.

Thanks for your suggestion. We appreciate this point and agree that clearer guidance on how to interpret the temporal and scaling properties of the tensor components would help readers. In the TCA framework, each component is defined by three separable factors: a neuron factor, a temporal factor, and a trial (position) factor. The temporal factor reflects the shape of the activity pattern within a trial, indicating when during the trial that component is expressed, whereas the trial factor reflects how strongly that temporal pattern is expressed at each position and across trials.

Importantly, the absolute scaling of these factors is not independently meaningful. Because TCA components are scale-indeterminate, the magnitude of the temporal factor and the trial factor should be interpreted relative to one another within a component, not across components. Thus, a large value in the trial factor does not imply stronger neural activity per se, but rather greater expression of that component’s characteristic temporal pattern at that position or trial.

Accordingly, when a component shows similar temporal dynamics across groups but differs in its trial factor structure—as observed here—the interpretation is that the same within-trial dynamics are being differentially recruited across task positions, rather than that the timing of neural responses has changed.

We have added a brief discussion of this in this section of the results in the manuscript.

(5) Sucrose control

Sucrose self-administration is a reasonable control for instrumental experience and reward exposure, but it means that this group also acquired an additional task involving the same reinforcer. This experience may itself influence OFC representations and could contribute to the generalization observed in control animals. A brief discussion of this possibility would help contextualize the interpretation of cocaine-related effects.

We agree that sucrose self-administration is not a perfect neutral manipulation and that this experience could, in principle, influence OFC representations. In particular, sucrose self-administration involves instrumental responding for the same primary reinforcer used in the odor task, and thus may promote additional learning about reward predictability, action–outcome contingencies, or contextual structure that could facilitate generalization.

Several considerations, however, suggest that the generalization observed in control animals primarily reflects learning-dependent refinement of task representations rather than a specific consequence of sucrose self-administration per se. First, the amount of sucrose administered during this phase was minimal (50 µl × 60 presses at most per session for 14 sessions) compared with the total sucrose reward obtained during task recording (100 µl × 160 trials per session for several dozen sessions). Second, all rats were extensively trained on the odor sequence task prior to any self-administration, and the key signatures of compression and generalization we report—near-chance discrimination between functionally equivalent positions—are consistent with prior studies using the same task in animals that did not undergo sucrose self-administration. Finally, comparisons to less-trained animals in earlier work show that OFC representations evolve toward greater abstraction with increasing task experience, indicating that generalization is a property of advanced learning rather than a unique outcome of sucrose exposure.

Importantly, even if sucrose self-administration were to enhance generalization in OFC, this would not account for the primary finding that cocaine-experienced rats fail to show these signatures despite identical task training and parallel instrumental experience. Thus, the critical comparison is not between sucrose-trained animals and naive controls, but between two groups matched for self-administration experience, differing only in the pharmacological consequences of the reinforcer. Within this framework, the absence of position-general representations in cocaine-experienced rats reflects a disruption of normal learning-dependent abstraction rather than an artifact of the control condition.

We have added a brief discussion acknowledging that sucrose self-administration may bias OFC toward abstraction, while emphasizing that cocaine exposure prevents the emergence or maintenance of these representations under otherwise comparable experiential conditions.

(6) Acknowledge low N

The number of rats per group is relatively low. Although the effects appear consistent across animals within each group, this sample size does not fully rule out idiosyncratic, animal-specific effects. This limitation should be explicitly acknowledged in the manuscript.

We acknowledge that the number of animals per group is relatively small and therefore cannot fully rule out animal-specific effects. However, the key neural and behavioral signatures reported here were consistent across individual animals within each group and across multiple levels of analysis, and no outliers were observed. In addition, sample sizes of this scale are common in cocaine self-administration studies due to their technical and logistical constraints. We did not attempt to obscure this limitation and have now explicitly acknowledged it in the manuscript discussion.

(7) Figure 3E-F: The task positions here are ordered differently (P1, P4, P2, P3) than elsewhere in the paper. Please reorder them to match the rest of the paper.

Thank you for pointing this out. We agree that the ordering of task positions in Figures 3E–F should be consistent with the rest of the manuscript. We have reordered the positions to match the standard sequence order used elsewhere in the paper (P1, P2, P3, P4) to improve clarity and avoid confusion.

Reviewer #2 (Public review):

In the current study, the authors use an odor-guided sequence learning task described as a "figure 8" task to probe neuronal differences in latent state encoding within the orbitofrontal cortex after cocaine (n = 3) vs sucrose (n = 3) self-administration. The task uses six unique odors which are divided into two sequences that run in series. For both sequences, the 2nd and 3rd odors are the same and predict reward is not available at the reward port. The 1st and 4th odors are unique, and are followed by reward. Animals are well-trained before undergoing electrode implant and catheterization, and then retrained for two weeks prior to recording. The hypothesis under test is that cocaine-experienced animals will be less able to use the latent task structure to perform the task, and instead encode information about each unique sequence that is largely irrelevant. Behaviorally, both cocaine and sucrose-experienced rats show high levels of accuracy on task, with some group differences noted. When comparing reaction times and poke latencies between sequences, more variability was observed in the cocaine-treated group, implying animals treated these sequences somewhat differently. Analyses done at the single unit and ensemble level suggests that cocaine self-administration had increased the encoding of sequence-specific information, but decreased generalization across sequences. For example, the ability to decode odor position and sequence from neuronal firing in cocaine-treated animals was greater than controls. This pattern resembles that observed within the OFC of animals that had fewer training sessions. The authors then conducted tensor component analysis (TCA) to enable a more "hypothesis agnostic" evaluation of their data.

Overall, the paper is well written and the authors do a good job of explaining quite complicated analyses so that the reader can follow their reasoning. I have the following comments.

While well-written, the introduction mainly summarises the experimental design and results, rather than providing a summary of relevant literature that informed the experimental design. More details regarding the published effects of cocaine self-administration on OFC firing, and on tests of behavioral flexibility across species, would ground the paper more thoroughly in the literature and explain the need for the current experiment.

We appreciate this suggestion and have tried to expand the Introduction to more explicitly situate the study within the existing literature on cocaine-induced changes in OFC function. In particular, prior work has shown that cocaine self-administration alters OFC firing properties and disrupts behavioral flexibility across species, including impairments in reversal learning, outcome devaluation, and sensory preconditioning. We have revised the Introduction to expand this literature review and more clearly articulate how these established findings motivated our focus on OFC representations of hidden task structure and generalization.

For Fig 1F, it is hard to see the magnitude of the group difference with the graph showing 0-100%- can the y axis be adjusted to make this difference more obvious? It looks like the cocaine-treated animals were more accurate at P3- is that right?

The concluding section is quite brief. The authors suggest that the failure to generalize across sequences observed in the current study could explain why people who are addicted to cocaine do not use information learned e.g. in classrooms or treatment programs to curtail their drug use. They do not acknowledge the limitations of their study e.g. use of male rats exclusively, or discuss alternative explanations of their data.

We agree that the current 0–100% scale can make small differences difficult to discern. We will make it clear in the figure captions (We will adjust the y-axis to a narrower range to better highlight group differences). Across P3, cocaine-experienced rats were more accurate than controls.

We appreciate the suggestion to expand the discussion. We have revised the concluding section to acknowledge key limitations, including the use of only male rats, the number of subjects, and to note that alternative explanations—such as differences in motivational state or attention—could also contribute to the observed effects. These revisions provide a more balanced interpretation while retaining the focus on OFC-mediated generalization as a potential mechanism for persistent, context-specific drug-seeking.

Is it a problem that neuronal encoding of the "positions" i.e. the specific odors was at or near chance throughout in controls? Could they be using a simpler strategy based on the fact that two successive trials are rewarded, then two successive trials are not rewarded, such that the odors are irrelevant?

We thank the reviewer for this point. While neuronal encoding of individual positions (specific odors) in control animals was comparatively lower, this does not indicate that the rats were using a simpler strategy based solely on reward patterns. First, rats were extensively trained on the odor sequence task prior to recordings, demonstrating accurate discrimination across all positions, and their trial-by-trial behavior reflects sensitivity to specific odors rather than only reward alternation. Second, the task design—with overlapping sequences and positions that differ in reward contingency across sequences—requires tracking odor-specific context to maximize reward; a purely “two rewarded, two non-rewarded” strategy would fail at overlapping positions and would not account for the compression of functionally equivalent positions observed in the OFC. Third, in the less-trained rats shown in Figure 3C, decoding accuracy was higher than in the sucrose group, indicating that these animals still differentiated negative positions. With additional training, decoding patterns suggested improved generalization across positions. Thus, the near-chance neural selectivity in controls reflects representation of latent task states rather than external sensory cues, consistent with the idea that OFC abstracts task-relevant structure and ignores irrelevant sensory differences.

When looking at the RT and poke latency graphs, it seems the cocaine-experienced rats were faster to respond to rewarded odors, and also faster to poke after P3. Does this mean they were more motivated by the reward?

At present, the basis of these response-time differences remains unclear, in part because motivation is difficult to define operationally. If motivation is indexed solely by reaction time or poke latency, then the data are consistent with increased response vigor in cocaine-experienced rats. Indeed, RT and poke-latency measures indicate that cocaine-experienced rats responded more quickly on some rewarded trials, including after P3. However, overall task performance was high in both groups, suggesting that these differences cannot be attributed simply to superior learning or engagement. Faster responses may also reflect differences in deliberation or strategy, with cocaine-experienced rats relying more on rapid, stimulus-driven responding and sucrose-trained rats engaging in more careful evaluation. In addition, altered reward sensitivity or persistent effects of cocaine exposure may contribute to these behavioral differences. Thus, the faster responses observed in cocaine-experienced rats likely reflect a combination of heightened reward responsivity and altered encoding of task structure, rather than a straightforward increase in motivation alone.

Recommendations for the authors:

The reviewers were very positive about the manuscript and emphasized the rigor and state of the art analyses. Two points that came up were the very small n (6 total and 3 per condition) and the exclusive use of males. Adding more subjects is not recommended. However, more discussion and acknowledgement of this issue is recommended. The main concern is that idiosyncratic differences between individuals (not differences in cocaine history) are responsible for the differences observed in OFC encoding.

We acknowledge that the sample size (n = 3 per group) and use of only male rats limit generalizability and do not fully rule out idiosyncratic, individual-specific effects. However, the key neural and behavioral signatures we report were consistent across all animals within each group and across multiple analyses (single-unit, ensemble decoding, and TCA). We now explicitly note these limitations in the Discussion, emphasizing that while individual variability cannot be fully excluded, the convergence of results across multiple levels of analysis supports the interpretation that the observed differences reflect effects of prior cocaine exposure rather than idiosyncratic differences.

Reviewer #2 (Recommendations for the authors):

In the legend to figure 2, the authors state "Notably, rats could discriminate between the two sequences (S1 vs. S2) based solely on current sensory information at two task epochs ["Odor" at P3 and P4; black bars]. At all other task epochs, indicated by gray bars, the discrimination relied on an internal memory of events". I'm confused by this statement- how does the odor at P3 help to discriminate the sequences? Surely P1 and P4 are the times when the odor sampling indicates which sequence they are in?

We thank the reviewer for pointing out this source of confusion. The statement in the original figure legend was imprecise, and we have removed the figure and revised the figure legends because the results in the left panel substantially overlapped with those shown in the right panel. In this task, odors at positions P1 and P4 are the only cues that directly signal sequence identity, whereas the odors presented at P2 and P3 are identical across sequences. Accordingly, discrimination observed during the “Odor” epoch at P3 does not reflect sensory differences but instead depends on the animal’s use of internal memory or sequence context to infer sequence identity.

Author response:

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

Reviewer #1:

Yet I think that important aspects of my critique of the first statement of the manuscript about the flaws of [SR] model remain unanswered.

I believe that I have fully addressed the points in the earlier review. The reviewer had doubted that my results were correct, attributing them to “a poor setup of the model” on my part. The reviewer stated that if I were correct about the factor of >10⁴³ change in cmax, this would “naturally break down all the estimates and conclusions made in Siljestam and Rueffler” (S&R).

It appears that the reviewer is now convinced that my results represent a faithful analysis of the models on which S&R based their claims. The reviewer now contends that these results, including the factor of >10⁴³, present no difficulties for the claims of S&R after all. In fact, this enormous factor of >10⁴³ is now claimed to support the conclusions of S&R by invalidating my conclusions. I respond to these new and very different arguments in what follows.

As I stated in the first round of review, the issue is not the enormity of this factor per se, but the fact that the compensatory adjustment of cmax conceals the true effects of changes in other parameters. These effects are large; small changes to the parameter values mostly eliminate the diversity that the model is claimed to explain.

The model in [SR] is not phenomenological as none of the parameters or functional forms were derived empirically. Instead, it is a proof of principle demonstration that inevitably grossly simplifies the actual immune response.

The hidden sensitivity of the results of S&R to paramater values is sufficient to invalidate them as a proof of principle. The manuscript goes further and explains how the problem "is not specific to the details of the models of Siljestam and Rueffler, but is inherent in the phenomenon invoked to allow high diversity" because "any change that affects condition by as much as the difference between MHC heterozygotes and homozygotes will eliminate high equilibrium diversity". This general principle addresses all of the reviewer's points.

In reality, a new pathogen cannot reduce the "survival" by such a factor as it would wipe out any resident population. So to compensate for such an artifact, the additional factor cmax was introduced to buffer such an excess. There is no reason to fix cmax once for an arbitrary number of pathogens, because varying cmax basically reflects the observation that a well-adapted individual must have a reasonable survival probability.

This is not a legitimate reason for making compensatory, diversity-promoting adjustments to cmax when evaluating sensitivity to other parameters. If the number of pathogens or their virulence changes, cmax obviously does not automatically change along with it. If the population or species consequently goes extinct, then it goes extinct. If it persists, it does so with the same value of cmax.

The possibility of extinction arguably puts a minimum value on cmax, but it does not restrict it to a range of values that conveniently leads to high MHC diversity. In the examples that I analyzed, slightly decreasing the number of pathogens or their virulence, which increases survivability, eliminates diversity. This phenomenon obviously cannot be dismissed on the grounds that survivability would be too low for the species to exist.

S&R in effect assume that the condition of the most fit homozygote remains fixed, regardless of the number of pathogens, their virulence, and myriad other differences between species. It is this assumption that is without justification.

At the same time, there are many ways in which the numerical simulation may break down when the survival rates become of the order of 10^(-43) instead of one

I am not sure what is meant by “the numerical simulation may break down”. Numerical error is not a tenable explanation of the lack of diversity observed in that simulation. The outcome is exactly what is expected from purely theoretical considerations: conditions of all genotypes fall on the steep part of the curve, making the mechanism proposed by S&R largely inoperative, so a pair of alleles forming a fit heterozygote comes to predominate. The numerical simulation is actually superfluous.

Low survival rates are completely irrelevant to the effect of decreasing the number of pathogens or their virulence, which does not lower survival rates, but does eliminate diversity.

so it comes to no surprise that the diversification, predicted by the adaptive dynamics, does not readily occur in the scenario with an addition or removal of the 8th pathogen with a very high virulence \nu=20.

Whether or not it surprising, the lack of diversity is a problem for the claims of S&R, as there is no reason to expect the number of pathogens to have just the right value to produce high diversity. Furthermore, for many combinations of values of the other parameters (e.g., my v=19.5 and 20.5 examples), no number of pathogens leads to high diversity.

Again, the general principle mentioned above makes the details that the reviewer refers to irrelevant. Nonetheless, some additional remarks are in order:

(1) This comment ignores the fact that removal of a pathogen, or a slight decrease in “virulence”, eliminates diversity without lowering survival rates.

(2) Small increases or decreases in v (virulence) eliminate diversity without having such large effects on condition.

(3) In the example emphasized by the reviewer, mean survival rates are nowhere near as low as 10^-43. Only homozygotes have such low fitness.

(4) The adaptive dynamics predict the low diversity seen in the simulations, contrary to what the reviewer seems to suggest. Elimination of diversity is not an artifact of the simulation.

(5) v\=20 was chosen because it is most favorable to the model of S&R in that it yields the highest diversity. Indeed, S&R only observed realistically high diversity with the narrow gaussians that the reviewer objects to. With lower values of v, diversity is much lower, but even this meager diversity is eliminated by small changes in parameter values (see below). If narrow gaussians and large effects of pathogens somehow invalidate results, then they invalidate the high-diversity results of S&R.

I have doubts that the reported breakdown of the [SR] model with fixed cmax remains observable with less extreme values of m and \nu (say, for \nu=7 and m=3 plus or minus 1 used in Fig. 3 in the manuscript).

These doubts are unwarrented. With the suggested parameter values, for example, increasing or decreasing m by 1 reduces the effective number of alleles to around 1 or 2. This can easily be checked using the simulation code of S&R, as detailed in my initial response and now in a Supplementary Text. Even without this result, the general principle mentioned above tells us that considering other regions of parameter space cannot rescue the conclusions of S&R.

So I still find the claim that " the phenomenon that leads to high diversity in the simulations of Siljestam and Rueffler depends on finely tuned parameter values" is not well substantiated.

What is unsubstantiated is the claim of S&R that “For a large part of the parameter space, more than 100 and up to over 200 alleles can emerge and coexist”. As my manuscript illustrates, this is an illusion created by the adjustment of one parameter to compensate for changes in others.

The reviewer even acknowledges that “the choice of constants and functions...works in a limited range of parameter values”. Furthermore, the manuscript explains why this problem is inherent to the general phenomenon, not specific to the details of the model or parameter values.

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

Public Reviews:

Reviewer #1 (Public review):

It appears obvious that with no or a little fitness penalty, it becomes beneficial to have MHC-coding genes specific to each pathogen. A more thorough study that takes into account a realistic (most probably non-linear in gene number) fitness penalty, various numbers of pathogens that could grossly exceed the self-consistent fitness limit on the number of MHC genes, etc, could be more informative.

The reviewer seems to be referring to the cost of excessively high presentation breadth. Such a cost is irrelevant to the inferior fitness of a polymorphic population with heterozygote advantage compared to a monomorphic population with merely doubled gene copy number. It is relevant to the possibility of a fitness valley separating these two states, but this issue is addressed explicitly in the manuscript.

An addition or removal of one of the pathogens is reported to affect "the maximum condition", a key ecological characteristic of the model, by an enormous factor 10^43, naturally breaking down all the estimates and conclusions made in [RS]. This observation is not substantiated by any formulas, recipes for how to compute this number numerically, or other details, and is presented just as a self-standing number in the text.

It is encouraging that the reviewer agrees that this observation, if correct, would cast doubt on the conclusions of Siljestam and Rueffler. I would add that it is not the enormity of this factor per se that invalidates those conclusions, but the fact that the automatic compensatory adjustment of c</sub>max</sub> conceals the true effects of removing a pathogen, which are quite large.

I am not sure why the reviewer doubts that this observation is correct. The factor of 2.7∙10⁴³ was determined in a straightforward manner in the course of simulating the symmetric Gaussian model of Siljestam and Rueffler with the specified parameter values. A simple way to determine this number is to have the simulation code print the value to which c</sub>max</sub> is set, or would be set, by the procedure of Siljestam and Rueffler for different parameter values. I have in this way confirmed this factor using the simulation code written and used by Siljestam and Rueffler. A procedure for doing so is described in the new Supplementary Text S1. In addition, I now give a theoretical derivation of this factor in Supplementary Text S2.

This begs the conclusion that the branching remains robust to changes in cmax that span 4 decades as well.

That shows at most that the results are not extremely sensitive to c</sub>max</sub> or K. They are, nonetheless, exquisitely sensitive to m and v. This difference in sensitivities is the reason that a relatively small change to m leads to such a large compensatory change in c</sub>max</sub>. It is evident from Fig. 4 of Siljestam and Rueffler that the level of diversity is not robust to these very large changes in c</sub>max</sub>, which include, as noted above, a change of over 43 orders of magnitude.

As I wrote above, there is no explanation behind this number, so I can only guess that such a number is created by the removal or addition of a pathogen that is very far away from the other pathogens. Very far in this context means being separated in the x-space by a much greater distance than 1/\nu, the width of the pathogens' gaussians. Once again, I am not totally sure if this was the case, but if it were, some basic notions of how models are set up were broken. It appears very strange that nothing is said in the manuscript about the spatial distribution of the pathogens, which is crucial to their effects on the condition c.

I did not explicitly describe the distribution of pathogens in antigenic space because it is exactly the same as in Siljestam and Rueffler, Fig. 4: the vertices of a regular simplex, centered at the origin, with unity edge length.

The number in question (2.7∙10⁴³) pertains to the Gaussian model with v\=20. As specified by Siljestam and Rueffler, each pathogen lies at a distance of 1 from every other pathogen, so the distance of any pathogen from the others is indeed much greater than 1/v. This condition holds, however, for most of the parameter space explored by Siljestam and Rueffler (their Fig. 4), and for all of the parameter space that seemingly supports their conclusions. Thus, if this condition indicates that “basic notions of how models are set up were broken”, they must have been broken by Siljestam and Rueffler.

...the branching condition appears to be pretty robust with respect to reasonable changes in parameters.

It is clear from Fig. 4 of Siljestam and Rueffler that the branching condition is far from sufficient for high MHC diversity.

Overall, I strongly suspect that an unfortunately poor setup of the model reported in the manuscript has led to the conclusions that dispute the much better-substantiated claims made in [SD].

The reviewer seems to be suggesting that my simulations are somehow flawed and my conclusions unreliable. I have addressed the reasons for this suggestion above. Furthermore, I have confirmed the main conclusion—the extreme sensitivity of the results of Siljestam and Rueffler to parameter values--using the code that they used for their simulations, indicating that my conclusions are not consequences of my having done a “poor setup of the model”. I now describe, in Supplementary Text S1, how anybody can verify my conclusions in this way.

Reviewer #2 (Public review):

(1) The statement that the model outcome of Siljestam and Rueffler is very sensitive to parameter values is, in this form, not correct. The sensitivity is only visible once a strong assumption by Siljestam and Rueffler is removed. This assumption is questionable, and it is well explained in the manuscript by J. Cherry why it should not be used. This may be seen as a subtle difference, but I think it is important to pin done the exact nature of the problem (see, for example, the abstract, where this is presented in a misleading way).

I appreciate the distinction, and the importance of clearly specifying the nature of the problem. However, as I understand it, Siljestam and Rueffler do not invoke the implausible assumption that changes to the number of pathogens or their virulence will be accompanied by compensatory changes to c</sub>max</sub>. Rather, they describe the adjustment of c</sub>max</sub> (Appendix 7) as a “helpful” standardization that applies “without loss of generality”. Indeed, my low-diversity results could be obtained, despite such adjustment, by combining the small change to m or v with a very large change to K (e.g., a factor of 2.7∙10⁴³). In this sense there is no loss of generality, but the automatic adjustment of c</sub>max</sub> obscures the extreme sensitivity of the results to m and v.

(2) The title of the study is very catchy, but it needs to be explained better in the text.

I have expanded the end of the Discussion in the hope of clarifying the point expressed by the title.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I would like to suggest to the author that they provide essential details about their simulations that would justify their claims, and to communicate with Mattias Siljestam and Claus Rueffler whether claims of the lack of robustness could be confirmed.

The models simulated were modified versions of those of Siljestam and Rueffler. Thus, only the modifications were described in my manuscript. I have added a more detailed description of how c</sub>max</sub> was set in the simulations concerned with sensitivity to parameter values. In addition, the new Supplementary Text S1, which describes confirmation of the lack of robustness using the code of Siljestam and Rueffler, should remove any doubt about this conclusion.

Reviewer #2 (Recommendations for the authors):

I have no further recommendations. The manuscript is well written and clear.

Thank you.

Reviewer #3 (Recommendations for the authors):

(1) Since this is a full report and not just a letter to the editor, it would benefit from a bit more introduction of what the MHC actually is and what the current understanding of its evolution is. Currently, it assumes a lot of knowledge about these genes that might not be available to every reader of eLife.

I have added some more information to the opening paragraph. I would also note that this report was submitted as a “Research Advance”, which may only need “minimal introductory material”.

(2) Some more recent literature on MHC evolution should be added, e.g., the review by Radwan et al. 2020 TiG, a concrete case of MHC heterozygote advantage by Arora et al. 2020 MolBiolEvol, and a simulation of MHC CNV evolution by Bentkowski et al. 2019 PLOSCompBiol.

I have cited some additional literature.

(3) Since much of the criticism hinges on the cmax parameter, its biological meaning or role (or the lack thereof) could be discussed more.

I am not sure what I can add to what is in the first paragraph of the Discussion.

(4) I find it difficult to grasp how the v parameter, which is intended to define pathogen virulence, if I understand it correctly, can be used to amend the breadth of peptide presentation. Maybe this could be illustrated better.

I have attempted to make this clearer. The parameter v actually controls the breadth of peptide detection conferred by an allele, which, if not identical to the breath of presentation, is certainly affected by it. The basis of the “virulence” interpretation seems to be that narrower detection breadth can, according to the model, only decrease peptide detection probability, which increases the damage done by pathogens.

(5) Please check sentences in lines 279ff on peptide detection and cost of . There seem to be words missing.

There was an extraneous word, which I have removed. Thank you for pointing this out.

Reviewer #1 (Public review):

Summary:

This study examined whether infraslow fluctuations in noradrenaline and in heart rate are coupled and how they are affected by sleep transitions. The authors used the fluorescent NA biosensor GRAB-NE2m in the medial prefrontal cortex of mice to record extracellular NA while also recording EEG and EMG during sleep-wake episodes. They also analyzed previously published human data to reproduce relationships they found between sigma power and RR intervals in mice.

Strengths:

This is an impressive study with significant strengths, as it involves a rich set of data that includes not only observations of associations between heart rate and noradrenergic dynamics but also optogenetic manipulation of the locus coeruleus. Human data is presented to show parallels in the association between sigma power during sleep and phasic heart-rate bursts.

Weaknesses:

(1) Language could be clearer and more precise. As detailed below, in both the introduction and the discussion, the way the hypotheses and study objectives are described could use some revision to be more precise and accurate.

1A) In the introduction on p. 4: The overarching question is framed as "could the peripheral autonomous systems be a read-out of the central LC-NE system and thus be a biomarker of memory consolidation and LC dysfunction?" This gives the impression that the LC function would be the main influence on peripheral autonomous systems. There are, of course, many influences on peripheral autonomous systems, so it would be advisable for the authors to be more specific here about what signal(s) in particular would be predicted to be sensitive markers of LC function.

1B) In the discussion on p. 12: "In this study, we leveraged real-time measurements of mPFC NE levels and HR measurements from EMG recordings in mice to investigate the causal link between the two variables with high temporal resolution in freely moving sleeping mice, with similar inspection in humans." To test the causal link between mPFC NA levels and HR measures, the study would manipulate NA levels just in the mPFC and not elsewhere in the brain. However, in this study, the manipulation occurred in the LC, and so there would be broad cortical changes in NA levels. Thus, it could be that LC activity causes HR changes via a non-PFC pathway.

(2) Comparisons with the control condition need further development.

2A) While the authors did include a key YFP control condition, in the main text no direct statistical comparison between the closed-loop optogenetic stimulation (ChR2) condition and the YFP control condition was reported. (It was reported in Supplementary Figure 2c-d.) Instead, in the main text, the authors only reported that the effects of stimulation were significant in the closed-loop condition and not in the control. However, that is not the same as demonstrating that the two conditions significantly differed from each other, and it is the direct test that is important for the conclusions, so it seems important to include this result in the main presentation.

2B) In addition, the authors should address the issue that the pre-stimulation NE was consistently significantly lower in the YFP condition than in the ChR2 condition (see Supplementary Figure 2c), which is a potential confound.

2C) Direct comparison of the strengths of correlations shown in Figure 2h vs. Supplementary Figure 2f should be included. Currently, we see relatively weak correlations in both ChR2 and YFP conditions, and it is not clear if the relationships differ in the control. It seems they are still present in the control condition but weaker, which would contradict the apparently broad claim on p. 7 that "No such effects were present in the control condition" (it is not entirely clear whether this claim refers to all effects discussed in the figure or just a subset - this language should be clarified).

2D) Did the YFP controls vs. ChR2 animals show any differences in the number of NA states that triggered stimulation in the closed-loop system? With ChR2 animals, stimulation changes NA, which could change future triggering. In YFP animals, nothing changes NA (other than natural fluctuations), so the dynamics of stimulation timing could diverge between groups in a way that complicates interpretation. Specifically, if ChR2 stimulation raises NA and prevents future threshold crossings, ChR2 animals may end up receiving fewer subsequent stimulations than YFP animals (or a different temporal clustering). If the number or pattern of stimulation differed in two groups, it would be important to have a yoked control where matched animals get the same stimulation pattern but not triggered by their own NA.

(3) Some more discussion/explanation of the rationale for the closed-loop approach and how it influences how we should interpret the results could be useful. For instance, currently, it is not clear whether LC stimulation needs to be timed after an NA dip to yield the effects seen.

(4) The section on heart rate decelerations is hard to follow. In particular, I was not sure how to interpret Figure 3f-j. For Figure 3f, what does the middle line represent? The laser onset or the max RR value after laser onset? What is the baseline that is used to correct the values to obtain amplitudes? If it is the whole period before the maximal RR value or the laser onset, wouldn't baseline values differ significantly across conditions and so potentially account for differences seen between conditions in the reported HR decelerations? Larger HR decelerations may be seen in conditions with higher HR simply as a regression to the mean phenomenon.

(5) The findings regarding LC suppression could be further clarified.

5A) Page 8: "observed a response in NE decline" - please be more precise. Did NE decline more or less?

5B) It would be helpful to also show the correlation between NE and RR in the control (YFP) condition and whether there were any differences between YFP and Arch conditions (Figure 4e).

5C) This sentence took me multiple readings to understand - it would be helpful to rewrite to make it clearer: "indicating that, while HR generally did not respond strongly to LC suppression, the variability in RR responses was dependent on NE changes to the suppression (Figure 4e)."

5D) The two colors in Figure 4 are similar and hard to distinguish.

5E) The correlations shown in Figure 4j seem to be driven by just two of the cases. Are the effects significant when outliers are removed?

5D) Page 10: Were there any differences in memory performance between the Arch and YFP conditions?

5E) Page 10: "We found a correlation between RR responses to LC suppression and sigma power, suggesting that a stronger HR reduction response is linked to higher spindle power." It should be noted in the text that the correlation was not specific to sigma (it was also seen for theta and beta, Figure 4i).

(6) It is not clear which of the sigma power and RR interval findings do/do not exactly line up between the mice and humans. It could be helpful to have a table comparing them. For instance, was the finding in humans that pre-HRB sigma power was positively associated with slowing in heart rate after the HRB also seen in mice? Was there evidence in mice (as seen in the human sample) that sleep-dependent memory improvement was associated with pre-HRB sigma power?

(7) Page 18: It is not clear if the sex of mice was balanced across controls and optogenetics groups.

Reviewer #1 (Public review):

Summary:

Liao et al. performed a large-scale integrative analysis to explore the function of two cancer genes (BRCA1 and BRCA2) in lung cancer, which is one of the cancers with an extremely high mortality rate. The detailed genetic analysis demonstrated new roles of BRCA1/2 in causing the tumor microenvironment in lung cancer. In particular, the discovery of different mechanisms of BRCA1 and BRCA2 provides an essential foundation for developing drugs that target BRCA1 or BRCA2 in lung cancer therapy.

Strengths:

(1) This study leveraged large-scale genomic and transcriptomic datasets to investigate the prognostic implications of BRCA1/2 mutations in LUAD patients (~2,000 samples). The datasets range from genomics to single-cell RNA-seq to scTCR-seq.

(2) In particular, the scTCR-seq offers a powerful approach for understanding T cell diversity, clonal expansion, and antigen-specific immune responses. Leveraging these data, this study found that BRCA1 mutations were associated with CD8+ Trm expansion, whereas BRCA2 mutations were linked to tumor CD4+ Trm expansion and peripheral T/NK cell cytotoxicity.

(3) This study also performed a comprehensive analysis of genomic variation, gene expression, and clinical data from the TCGA program, which provides an independent validation of the findings from LUAD patients newly collected in this study.

(4) This study provides an exemplary integration analysis using both computational biology and wet bench experiments. The experimental testing in the A549 cell line further supports the robustness of the computational analysis.

(5) The findings of this study offer a comprehensive view of the molecular mechanisms underlying BRCA1 and BRCA2 mutations in LUAD. BRCA1 and BRCA2 are two well-known cancer-related genes in multiple cancers. However, their role in shaping the tumor microenvironment, particularly in lung cancer, is largely unknown.

(6) By focusing on PD-L1-negative LUAD patients, this study demonstrated the molecular mechanisms underlying resistance to immune therapy. These new insights highlight new opportunities for personalized therapeutic strategies to BRCA-driven tumors. For example, they found histone deacetylase (HDAC) inhibitors consistently downregulated 4-R genes in A549 cells.

(7) The deposition of raw single-cell sequencing (including scRNA-seq and scTCR-seq) data will provide an essential data resource for further discovery in this field.

Weaknesses:

(1) The finding of histone deacetylase (HDAC) inhibitors suggests the potential roles of epigenetic regulation in lung cancer. It would be interesting to explore epigenetic changes in LUAD patients in the future.

(2) For some methods, more detailed information is needed.

(3) There are grammar issues in the text that need to be fixed.

(2) Some text in the figures is not labeled well.

Author response:

eLife Assessment

This important study investigates the impact of BRCA1/2 mutations on immunotherapy in lung adenocarcinoma using multi-omics approaches. The detailed genetic analysis of two cancer genes (BRCA1 and BRCA2) demonstrated new roles for these genes in causing the tumor microenvironment in lung cancer. Further experimental explorations of the immune-related changes may still be required. The solid findings of this study provide a foundation for further developing drugs targeting BRCA1/2 in lung cancer therapy.

We would like to express our sincere gratitude for your thoughtful and constructive comments on our manuscript. We will carefully consider each comment from these two reviewers and will revise the manuscript accordingly. Below, we provide a point-by-point response to each comment.

Reviewer #1 (Public review):

Summary:

Liao et al. performed a large-scale integrative analysis to explore the function of two cancer genes (BRCA1 and BRCA2) in lung cancer, which is one of the cancers with an extremely high mortality rate. The detailed genetic analysis demonstrated new roles of BRCA1/2 in causing the tumor microenvironment in lung cancer. In particular, the discovery of different mechanisms of BRCA1 and BRCA2 provides an essential foundation for developing drugs that target BRCA1 or BRCA2 in lung cancer therapy.

Strengths:

(1) This study leveraged large-scale genomic and transcriptomic datasets to investigate the prognostic implications of BRCA1/2 mutations in LUAD patients (~2,000 samples). The datasets range from genomics to single-cell RNA-seq to scTCR-seq.

(2) In particular, the scTCR-seq offers a powerful approach for understanding T cell diversity, clonal expansion, and antigen-specific immune responses. Leveraging these data, this study found that BRCA1 mutations were associated with CD8+ Trm expansion, whereas BRCA2 mutations were linked to tumor CD4+ Trm expansion and peripheral T/NK cell cytotoxicity.

(3) This study also performed a comprehensive analysis of genomic variation, gene expression, and clinical data from the TCGA program, which provides an independent validation of the findings from LUAD patients newly collected in this study.

(4) This study provides an exemplary integration analysis using both computational biology and wet bench experiments. The experimental testing in the A549 cell line further supports the robustness of the computational analysis.

(5) The findings of this study offer a comprehensive view of the molecular mechanisms underlying BRCA1 and BRCA2 mutations in LUAD. BRCA1 and BRCA2 are two well-known cancer-related genes in multiple cancers. However, their role in shaping the tumor microenvironment, particularly in lung cancer, is largely unknown.

(6) By focusing on PD-L1-negative LUAD patients, this study demonstrated the molecular mechanisms underlying resistance to immune therapy. These new insights highlight new opportunities for personalized therapeutic strategies to BRCA-driven tumors. For example, they found histone deacetylase (HDAC) inhibitors consistently downregulated 4-R genes in A549 cells.

(7) The deposition of raw single-cell sequencing (including scRNA-seq and scTCR-seq) data will provide an essential data resource for further discovery in this field.

Weaknesses:

(1) The finding of histone deacetylase (HDAC) inhibitors suggests the potential roles of epigenetic regulation in lung cancer. It would be interesting to explore epigenetic changes in LUAD patients in the future.

Thank you for your insightful comment. We fully agree that the specific situation of epigenetic dysregulation in LUAD needs to be explored. We believe that future investigations utilizing clinical specimens and animal models to map histone acetylation patterns and DNA methylation profiles will be crucial for identifying novel biomarkers and therapeutic targets unique to LUAD.

(2) For some methods, more detailed information is needed.

This is a valid point. We agree that additional details regarding are necessary for clarity and reproducibility. We will expand these method details in the revised manuscript.

(3) There are grammar issues in the text that need to be fixed.

We apologize for our irregular use of grammar. In the revised manuscript, we will carefully check the grammar and make corrections.

(4) Some text in the figures is not labeled well.

We appreciate the reviewers' comments. We will add labels to the revised version of the figures.

Reviewer #2 (Public review):

Summary:

This study investigates the impact of BRCA1/2 mutations on immunotherapy in lung adenocarcinoma using multi-omics approaches. The work highlights distinct roles of BRCA1 and BRCA2 mutations in shaping immune-related processes, and is logically structured with clearly presented analyses. However, the conclusions rely primarily on descriptive computational analyses and would benefit from additional immunological validation.

Strengths:

By integrating public datasets with in-house data, this study examines the impact of BRCA1/2 mutations on immunotherapy in lung adenocarcinoma from multiple perspectives using multi-omics approaches. The analyses are diverse in scope, with a clear overall logic and a well-organized structure.

Weaknesses:

The study is largely descriptive and would benefit from additional immunological experiments or validation using in vivo models. The fact that the BRCA1 and BRCA2 samples were each derived from a single patient also limits the robustness of the conclusions.

Thank you for this excellent suggestion. In the revised manuscript, we will supplement the additional immunological experiments or validation using in vivo models. In addition, we will elaborate on the limitations of our study in the Discussion section and provide reasonable explanations.

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

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Reply to the reviewers

We sincerely thank all the reviewers for their thoughtful and constructive comments.

In our revision, we have addressed the reviewer's specific criticisms with additional experiments and text edits as described below. We believe the constructive feedback from peer reviews helped us to significantly extend our mechanistic findings and strengthen the manuscript through revision.

Point-by-point description of the revisions

Reviewer #1:

Summary:

The study by Zatulovskiy et al. examined how cell size influences cell susceptibility to ferroptosis. The authors found a size dependence specifically for ferroptosis-inducing drug Era2, but not for other drugs. Using various human cell lines (HMEC, HT 1080, RPE 1), the authors generated populations of small and large G1 cells by FACS, CDK4/6 inhibition (palbociclib), or inducible cyclin D1 knockdown, and measured cell susceptibility to ferroptosis. Larger cells were more resistant than smaller cells. Mechanistically, larger cells showed reduced plasma membrane lipid peroxidation, higher glutathione concentrations, and changes in relevant cellular proteins levels, as analyzed using previously published data. Deleting ACSL4, which is involved in ferroptosis, partly eliminated the size dependence of ferroptosis. The work concludes that cell size is a key determinant of ferroptosis susceptibility.

My major concerns about this work focus on whether many of the results reflect cell size or cell cycle effects, and whether the FACS-based size-scaling analyses have some misleading features to their design & presentation. If these concerns can be addressed with new experiments, then the conclusions of this paper are justified. If these concerns cannot be addressed, then the authors should more directly acknowledge the alternative hypothesis that cell cycle effects may explain many of their results.

The experiments seem to be replicated sufficiently, and most conclusions rely on data from multiple cell lines. My minor comments focus on needs to provide statistics and method details, and on suggestions on how to improve text clarity, but these edits are easily done and don't require new experiments. Overall, this is an interesting study, and it should be published once the concerns below are addressed.

Major comments:

• In experiments reported in Fig 1 and 2A, the authors sort small and large cells in G1, plate them, and later start the drug treatments & cell monitoring. Are these cells actively cycling (progressing in the cell cycle), and how fast? The large cells are likely to enter S phase earlier than the small cells, so by the time that the authors start their drug treatments, they may be comparing cells in different cell cycle stages, which could influence drug sensitivity more than cell size (as the authors also suggest later in Fig 2). This needs to be controlled for. Furthermore, even if the cells remain in G1 after sorting until the drug treatments are started, the authors should address the fact that the drugs are present for a long time, thus targeting the cells in various cell cycle stages.

We agree with the reviewer that the cell cycle stage could affect ferroptosis susceptibility and could be a confounding effect in asynchronous cells. One of us (Dixon) reported the cell cycle effects on ferroptosis previously, and we observe them in this manuscript too (Fig. 2B,C,E). We now state this more clearly both in the Results and in the Discussion sections, where we write:

Line 159: "We note that non-arrested cells had a lower susceptibility to Era2-induced ferroptosis compared to cells that were arrested in G1 for 2-3 days, despite being smaller in size. This is likely due to the difference in the fraction of cells in different cell cycle phases between arrested and non-arrested conditions since cells in S/G2/M phases are known to be more resistant to ferroptosis than cells in G0/G1 phases (Rodencal et al, 2024; Kuganesan et al, 2023)"

Line 533: "Cells in G1 phase of the cell cycle were reported to be more susceptible to ferroptosis (Rodencal et al, 2024; Kuganesan et al, 2023), which suggested that ferroptosis inducers could be used in combination with cancer drugs, like the CDK4/6 inhibitor palbociclib, that arrest cells in G1 phase of the cell cycle (Herrera-Abreu et al, 2024). However, while CDK4/6 inhibitors arrest cells in G1, they do not inhibit cell growth, such that the longer they are arrested, the larger the cells grow (Lanz et al, 2022; Crozier et al, 2023; Manohar et al, 2023). This results in a complex, non-monotonic ferroptotic response dynamics in cells treated with CDK4/6 inhibitors (Fig. 2B,E). Just following CDK4/6 inhibitor treatment, as more and more cells are arrested in G1 phase, cells become more sensitive to both RSL3- and erastin-induced ferroptosis (Kuganesan et al, 2023; Rodencal et al, 2024). However, the longer the cells are arrested, the larger they become, which further promotes their susceptibility to RSL3 (Fig. S1B) but reduces their susceptibility to Era2-induced ferroptosis (Fig. 2B). The fact that the cell cycle arrest and cell size increase have opposing effects on Era2-induced ferroptosis susceptibility could explain why different studies reported seemingly contradictory results, where sometimes an increased and sometimes a decreased or unchanged sensitivity to system xc- inhibitors was observed depending on the cell type, duration and type of cell cycle arrest (Lee et al, 2024; Kuganesan et al, 2023; Rodencal et al, 2024). Such complex interplay between the cell cycle and cell size effects on ferroptosis suggests that combination therapies utilizing CDK4/6 inhibitors and ferroptosis inducers would have to carefully choose a dosage schedule.""

Given the potentially confounding effects of the cell cycle in cycling cells sorted by size, we performed an additional experiment, in which RPE-1 cells were pre-treated with the CDK4/6 inhibitor palbociclib to synchronize them in G1 phase prior to treatment. These cells were then continuously exposed to palbociclib during the Era2 treatment (Fig. 2C-E). RPE-1 cells pre-treated with palbociclib for 2 and 4 days had the same cell cycle distribution with 94% of cells being arrested in G1, but with different sizes. Cells treated with palbociclib for 4 days were significantly larger and more resistant to Era2 as can be seen in the Figure 2C-E.

Additionally, in the experiment shown in Fig. 5E,F, where we FACS-sorted WT and ACSL4 KO HMEC cells by cell size, and then measured Era2 susceptibility, we pre-treated the cells with palbociclib for 24 h to synchronize them in G1 prior to the sorting. We then cultured the cells in the presence of palbociclib during the Era2 treatment to avoid the cell cycle effects observed in Fig. 2. In this case, we still observe that larger cells are more resistant to Era2, consistent with our conclusion that cell size protects against Era2-induced ferroptosis.

Reviewer #1: "Can the G1 arrest-driven changes in drug susceptibility (Fig 2 C-D) be attributed to cell size? Can the authors rescue the palbociclib treatment with rapamycin or other growth inhibitors that allow size to remain small during G1 arrest?"

We have attempted to perform these experiments, but when we co-treated the cells with palbociclib and mTORC inhibitors, but observed variable results, which are likely due to the fact that prolonged mTORC inhibition itself rewires cellular metabolism and reduces cell susceptibility to ferroptosis, as one of us (Dixon) found previously (Armenta et al. (2022), Ferroptosis inhibition by lysosome-dependent catabolism of extracellular protein. Cell Chemical Biology 29: 1588-1600.e7). Our results were consistent with this previous report and is now included in a new supporting figure panel (Fig. S3C).

Thus, upon palbociclib+rapamycin co-treatment there seems to be a competition between cell-size-mediated and metabolism-mediated effects of mTORC inhibition on ferroptosis, which leads to variable outcomes.

Reviewer #1: "In Fig 2E-F, is the cell cycle distribution of the samples influenced by CCND1 shRNA induction? Are the drug sensitivity effects due to cell size or cell cycle changes?"

The CCND1 manipulation model is extensively characterized in our recent work cited in this manuscript (You et al. (2025), Cell size-dependent mRNA transcription drives proteome remodeling. 2025.10.30.685141 doi:10.1101/2025.10.30.685141). Indeed, CCND1 shRNA cells have a slightly elongated G1 phase due to a ~30% reduction in Cyclin D1 concentration: the G1 fraction changes from ~70% in wild-type to ~80% in CCND1 shRNA cells, which could potentially affect the ferroptosis susceptibility, but the additional results obtained on synchronized RPE-1 cells, described above (Fig. 2C-E), support the conclusion that the primary effect on Era2 sensitivity is due to cell size.

Reviewer #1: "Can the authors address the meaningfulness of the FACS-based size-scaling results in cases where cell-to-cell variability is very large? For example, in Fig 4D&G, the results are so variable even in identically sized cells that the importance of the size-scaling pattern seems questionable."

We do observe variability in fluorescent probe-based measurements of GSH and lipid oxidation, which could be due to biological (natural cell heterogeneity) and/or technical (low sensitivity of the probes) reasons. However, when we look at binned data and compare the mean values {plus minus} s.e.m. for each bin, we observe a robust and reproducible trend (black line with dark-grey shaded area), even though the SD is quite broad (lighter shaded area). We believe such trends are meaningful when describing cell death in probabilistic terms as we do. I.e., the GSH measurement might not be precise enough to predict cell death for a given individual cell, but the statistical trend is clear and these measurements help predict cell death probabilities for cells of different sizes.

Reviewer #1: "In Figs 4B-D, the cell size axis seems to have over 4-fold size variability, but when the authors show the analysis of this data (Figs 4E-G) the variability is only 2-fold. What was excluded and on what basis?"

To address this point, we have now clarified in the Methods section how the data were processed and what data points we excluded from this analysis:

Line 671: "For all binned flow cytometry data plots, the cells below the 2nd and above the 98th cell size percentiles were excluded to remove the extreme outliers. Then, the remaining data were binned by size and plotted as background-corrected average fluorescence intensity for each bin against the bin's average cell size. Bins with fewer than 200 cells were excluded from the analysis to reduce noise."

Typically, such pre-processing reduces the size range, mostly from the large-cell end, because of the long right tail of the size distribution containing a few very large cells.

Reviewer #1: "Based on the methods section & figure legends of Fig 4B-I, the RPE cells were not pre-sorted to include only G1 cells, nor did the assay account for cell cycle differences. How can these data be used to explain results from earlier figures, where analyses were exclusively focused on size differences in G1?"

This is a valid point: Cells in the GSH measurement experiment were not gated by Hoechst signal for G1 phase because the channel normally used for Hoechst staining was in this case occupied by the MCB probe. However, given the data in Fig. 4A,B showing that the GSH production machinery is superscaling when measured specifically in G1-phase cells, we believe the flow cytometry data in Fig. 4C-J showing GSH concentration increasing with cell size across the whole cell cycle is very likely true for G1 cells as well.

Reviewer #1: "Minor comments:

I recommend clarifying in the early introduction that all size changes discussed are in the absence of DNA content increase."

We have now clarified this in the introduction (Line 41 and Line 81).

Reviewer #1: "The introduction seems to cite primary research and review paper in the same sentences, which is a bit misleading as the reviews don't seem to add new evidence."

We have removed review citations where they did not provide additional context.

Reviewer #1: "*OPTIONAL* In the second introduction paragraph, consider the classification/description of the three different mechanisms. Currently, it seems that these mechanisms are not independent of each other, and the details provided about each mechanism are inconsistent."

We have now modified this paragraph to make the description more consistent.

Reviewer #1: "Please provide statistics for the IC50 values reported based on Fig 1C. Were small and large cells statistically different? Are the IC50 values reported as +/- standard deviation or some other metric?"

This has now been clarified in the text as follows:

"For example, at the 72 h time point, the Era2 IC50 was 28 {plus minus} 11 µM (mean {plus minus} SD) for large cells versus 2.0 {plus minus} 1.4 µM for small cells (Student's t-test: p = 0.039) (Fig. 1C)."

Reviewer #1: "*OPTIONAL* Providing more insight into why Era2 and RSL3 treatments yield more opposite responses would be of great interest to the field."

We agree this is an important point that should be discussed in more detail. In the field of ferroptosis, context-dependent (i.e., cell type-specific) effects are common and multiple groups including our own (Dixon) have published extensively on genes and mechanisms that can lead to differences between erastin2 and RSL3 sensitivity. For example, there are studies showing that the mTOR pathway or the p53 pathway can either prevent or promote ferroptosis, depending on the cell type and/or other currently unknown variables. To address more specifically the differences between Era2 and RSL3 in the context our observed cell-size-dependent response, we have now added more data and discussion. In the Results section we added panel 4B and the following text:

Line 359: "While the upregulation of GSH biosynthesis may promote the resistance of larger cells to ferroptosis, such an upregulation alone cannot explain why larger cells become more resistant to ferroptosis induced by the cystine import inhibitor Era2, but not, for example, by the GPX4 inhibitor RSL3 (Chan et al, 2025) (Figs. 2B, S1B). We found previously that upon mTORC1 inhibition cells can evade cystine deprivation-induced ferroptosis by uptake and catabolism of cysteine-rich extracellular proteins, mostly albumin (Armenta et al, 2022) (Fig. S3C). This process involves albumin degradation in lysosomes, predominantly by cathepsin B (CatB), and subsequent export of cystine from lysosomes to fuel the synthesis of glutathione. Large cells undergo proteome rearrangements similar to those occurring upon mTORC1 inhibition (Zatulovskiy et al, 2022). This suggests that large cells may upregulate CatB expression to bypass the Era2-induced cystine import inhibition via system xc-. To test this hypothesis, we used flow cytometry to measure how the expression of cathepsin B and the system xc- cystine/glutamate transporter SLC7A11 (xCT) scales with cell size (Fig. 4B). We found that SLC7A11 concentration modestly decreases, while CatB concentration significantly increases with cell size (Fig. 4B). This shift in the ratio between SLC7A11 and CatB supports the hypothesis that larger cells may rely less on cystine import via system xc- and thus become more resistant to system xc- inhibition by Era2."

Additionally, in the Discussion we added the following:

Line 578: "We show that large cells may become resistant specifically to Era2 but not RSL3 through the upregulation of lysosomal function, particularly cathepsin B expression, which enables the uptake and catabolism of cysteine-rich extracellular proteins. A size-dependent shift in the ratio between SLC7A11 and cathepsin B makes large cells less dependent on cystine import via system xc-, and thus, more resistant to Era2. In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

Reviewer #1: "Is the BODIPY-C11 labeling specific to plasma membrane, as suggested by the writing of the authors, or do the results shown integrate signals over all cell membranes?"

We thank the reviewer for pointing this out. BODIPY-C11 581/591 stains many membranes in the cell, not just the plasma membrane. We have changed the wording in the manuscript to reflect this.

Reviewer #1: "How exactly is gating done for the flow cytometry samples? Especially when analyzing size-scaling, the results are likely to be sensitive to outliers, such as those seen in Fig 4C (a subpopulation of very low CFSE stained cells). Can the authors clarify their methods and/or display supplementary figures with gating examples?"

We have now specified our gating strategy in the Methods section (Line 663) and added a corresponding Supplementary Figure S5:

"Single cells were gated based on FSC-A vs SSC-A, then FSC-A vs FSC-H, then SSC-A vs SSC-W plots. From this population of single cells, G1 cells were selected using Hoechst-A vs FSC-A plot for subsequent scaling analysis"

Reviewer #1: "In Fig 4, total protein staining was used as a control, whereas Fig 5B b-actin was used as a control. Why did the authors rely on different controls approaches for essentially the same measurements? Are these controls comparable?"

In our flow cytometry experiments, we consistently use live-cell total protein stain (CFSE) for live cells, and anti-Tubulin immunofluorescent staining for fixed cells, both of which scale in proportion to cell volume and act as a read-out for total cellular protein content (Lanz and Zatulovskiy et al., Mol Cell 2022; Berenson et al. MBoC 2019), which we use to calculate concentrations of other cellular components (analogous to loading controls). In Fig. 5B, beta-Actin is used as a reference - a protein whose concentration does not change with cell size, as opposed to ACSL4 whose concentration decreases with cell size. In this plot, both ACSL4 and beta-Actin amounts were normalized to alpha-Tubulin, which is analogous to a concentration calculation using loading control. This is now explained in more detail in the Figure legend.

Reviewer #2:

"Zatulovskiy et al. demonstrate that cell size modulates susceptibility to ferroptosis, a form of iron-dependent cell death driven by lipid peroxidation. Using human cell lines (HMEC, HT-1080, RPE-1), the authors examined cell size through FACS sorting, CDK4/6 inhibition and inducible cyclin D1 knockdown. They found that larger cells are more resistant to ferroptosis induced by system xc⁻ inhibition (erastin2), but more sensitive to GPX4 inhibition (RSL3), highlighting pathway-specific size dependencies.

Mechanistically, larger cells exhibited:

• Higher glutathione levels, supporting lipid peroxide detoxification
• Increased ferritin expression, promoting iron sequestration
• Lower ACSL4 levels, reducing incorporation of peroxidation-prone lipids These findings were supported by high-throughput microscopy, flow cytometry (BODIPY-C11 lipid peroxidation assays), and proteomic analyses. The study concludes that cell size influences proteome composition and metabolic capacity, thereby shaping cell death decisions, an insight with implications for aging, cancer, and ferroptosis-based therapies.

Major Comments

1. Direct evaluation of SLC7A11 abundance and function is needed The opposite size-dependent effects of erastin2 and RSL3 strongly suggest a role for SLC7A11/system xc⁻ activity in size-dependent ferroptosis resistance. However, SLC7A11 levels were not quantified due to insufficient peptide detection in the proteomic data.

o Direct measurement of SLC7A11 protein levels (immunoblotting or flow cytometry) in small vs large cells would test whether its expression scales with size.

o Functional perturbation (siRNA/CRISPR knockdown) followed by erastin2 treatment would provide mechanistic validation.

o Use of additional SLC7A11 inhibitors (e.g., sulfasalazine, sorafenib) could further test whether the size resistance phenotype is xc⁻-specific."

We agree that the difference in size-dependent responses to RSL3 and Era2 is an important point that needs further investigation and discussion, as other reviewers also pointed out. To address more specifically the differences between Era2 and RSL3 in the context of cell-size-dependent response, we have now added more data and discussion. In the Results section we added panel 4B measuring SLC7A11 and Cathepsin B scaling with cell size and the following text:

Line 359: "While the upregulation of GSH biosynthesis may promote the resistance of larger cells to ferroptosis, such an upregulation alone cannot explain why larger cells become more resistant to ferroptosis induced by the cystine import inhibitor Era2, but not, for example, by the GPX4 inhibitor RSL3 (Chan et al, 2025) (Figs. 2B, S1B). We found previously that upon mTORC1 inhibition cells can evade cystine deprivation-induced ferroptosis by uptake and catabolism of cysteine-rich extracellular proteins, mostly albumin (Armenta et al, 2022) (Fig. S3C). This process involves albumin degradation in lysosomes, predominantly by cathepsin B (CatB), and subsequent export of cystine from lysosomes to fuel the synthesis of glutathione. Large cells undergo proteome rearrangements similar to those occurring upon mTORC1 inhibition (Zatulovskiy et al, 2022). This suggests that large cells may upregulate CatB expression to bypass the Era2-induced cystine import inhibition via system xc-. To test this hypothesis, we used flow cytometry to measure how the expression of cathepsin B and the system xc- cystine/glutamate transporter SLC7A11 (xCT) scales with cell size (Fig. 4B). We found that SLC7A11 concentration modestly decreases, while CatB concentration significantly increases with cell size (Fig. 4B). This shift in the ratio between SLC7A11 and CatB supports the hypothesis that larger cells may rely less on cystine import via system xc- and thus become more resistant to system xc- inhibition by Era2."

Additionally, in the Discussion we added the following:

Line 578: "We show that large cells may become resistant specifically to Era2 but not RSL3 through the upregulation of lysosomal function, particularly cathepsin B expression, which enables the uptake and catabolism of cysteine-rich extracellular proteins. A size-dependent shift in the ratio between SLC7A11 and cathepsin B makes large cells less dependent on cystine import via system xc-, and thus, more resistant to Era2. In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

Reviewer #2: "2. Functional tests of ferritin contribution to resistance are needed

Although elevated ferritin (FTH1/FTL) levels in larger cells represent a strong correlational signal, definitive experimental evidence establishing causality is currently lacking.

o Measuring the labile iron pool directly in size-stratified populations would strengthen the link.

o Knockdown of FTH1 or FTL could reveal whether ferritin upregulation is necessary for the resistance of large cells to ferroptosis."

We thank the reviewer for raising this point. We have now completed additional experiments, as suggested by the reviewer, and found that iron chelation is unlikely to mediate the size-dependent response to Era2. We have modified the manuscript accordingly and added the following data and discussion to address this point:

Line 296: "The observed increase in ferritin concentration with cell size could therefore lead to additional Fe2+ ion chelation, which in turn would protect large cells from iron-dependent lipid peroxidation and ferroptosis. However, when we measured the concentration of labile intracellular Fe2+ using a fluorescent probe FerroOrange (Hirayama et al, 2020), we did not observe any size-dependent decrease in labile iron concentration (Fig. S2A). Previous work suggests a link between increased sequestration of ferrous iron in lysosomes and resistance to ferroptosis. It was reported that senescent cells, which are also large (Fig. S3A,B), gain resistance to ferroptosis through lysosomal alkalinization and sequestration of ferrous iron in lysosomes (Loo et al, 2025). We therefore tested whether the superscaling of lysosomes observed in large cells (Lanz et al, 2022; You et al, 2025) promotes Era2 resistance through lysosomal iron sequestration. To do this, we stained the cells with the lysosomal iron detection probe Lyso-FerroRed (Saimoto et al, 2025) and measured its scaling using flow cytometry (Fig. S2B). We observed that the amount of Lyso-FerroRed, and therefore, the amount of lysosomal iron, scaled in direct proportion to cell size, just like the total cellular protein content (Fig. S2B). These results indicate that iron chelation by ferritin and its sequestration in lysosomes are unlikely to play a crucial role in size-dependent decrease in Era2 sensitivity."

Reviewer #2: "3. Relevance to senescence should be addressed experimentally or explicitly discussed

Given that senescent cells are enlarged and accumulate in aged and tumour tissues, testing senescent models for erastin2 resistance would greatly strengthen the physiological significance."

We agree that an increase in cell size contributing to the resistance of senescent cells to ferroptosis is intriguing. We have now added a Supplementary Figure S3 and discussion of this point in the manuscript as follows:

Discussion line 552: "our data suggest that previously reported resistance of senescent cells to ferroptosis can at least partially be due to the increased cell size, a well-established hallmark of senescence."

Reviewer #2: "Minor Comments

1. Mechanistic nuance regarding RSL3 should be included RSL3 has been reported to induce ferroptosis independently of GPX4 (PMID: 37087975, PMID: 40392234) and may target other selenoproteins such as TXNRD1. This nuance would help explain the observed divergence between RSL3 and erastin2 sensitivity across sizes."

We have now added this in the Discussion as suggested by the reviewer (line 583):

"In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

Reviewer #2: "2. Dynamic range of BODIPY-C11 assays needs commentary

Despite high erastin2 doses, the oxidized BODIPY signal remains close to DMSO levels. The authors should comment on whether this reflects high GSH buffering capacity, probe limitations, or other factors."

We believe there are both technical (narrow dynamic range of the probe) and biological reasons for the relatively small (2-3 fold) difference in Oxidized-to-Non-oxidized BODIPY-C11 ratios between DMSO and Era2-treated cells. The biological reason is that the cells continue producing GSH until they fully deplete the cystine pool, which happens ~20-24 h after Era2 addition. Once the cystine pool is depleted, the cells very rapidly deplete GSH and initiate cell death. Therefore, there is only a short time window where cells are strongly depleted of GSH before dying. We see this small fraction of cells with a high Oxidized BODIPY-C11 signal in our flow cytometry experiments and in previous microscopy analysis of BODIPY-C11 (Murray et al., Protocol for detection of ferroptosis in cultured cells. STAR Protoc. 2023), but at our chosen time point (20h Era2) most cells are not as bright because we aimed to analyze the population before the onset of widespread cell death.

Reviewer #2: "3. Western blot for shCycD1 depletion should be included

CycD1 depletion usually causes cells to stop proliferating, which is not the case here. Therefore, depletion must be partial. The level of depletion should be shown by immunblotting."

The CCND1 manipulation model is extensively characterized in our recent work cited in this manuscript (You et al. (2025), Cell size-dependent mRNA transcription drives proteome remodeling. 2025.10.30.685141 doi:10.1101/2025.10.30.685141). CCND1 shRNA cells do not fully arrest in G0/G1 because the concentration of Cyclin D1 protein in this system is only partially decreased, as the reviewer noted. As a result, the cells have a slightly elongated G1 phase due to a ~30% reduction in Cyclin D1 concentration, but continue to proliferate. The G1 fraction changes from ~70% in wild-type to ~80% in CCND1 shRNA cells.

Reviewer #3:

"In this manuscript, Zatulovskiy and colleagues elaborate on their previous work describing cell size-dependent changes in the proteome by investigating whether these changes can be correlated in differences in cell physiology. Using a cleverly-designed high throughput screen, they searched for compounds that differently-sized cells display differential sensitivity towards. Their primary hit, Era2, is involved in the ferroptosis pathway and serves as the starting point for a detailed study of how excess cell size protects cells from ferroptosis-induced cell death via: 1) lower concentrations of ACSL4 (which produces peroxidation-prone PUFAs), 2) increased ferritin concentrations, and 3) increased GSH concentrations.

Overall, the experiments in this manuscript are well-designed and interpreted. It is an extremely well-written manuscript with a clear trajectory of logic. I have only a few major concerns that should be addressed before publication:"

We thank Reviewer #3 for their careful reading of the manuscript and for the clear summary of our study and its central findings. We appreciate their positive assessment of the experimental design, interpretation, and overall clarity of the writing and logical flow. We are also grateful for their constructive feedback and take their major concerns seriously; we have addressed each point in detail below.

Reviewer #3: "Major concerns:

1) In Figure 3E, the authors gate their flow cytometry data using SYTOX so that they are only analyzing live cells. Based on their gating scheme, it seems like there are really a lot of dead cells. Presumably the cells that died were the most sensitive to Era2, so it seems an oversight to discard these cells. Of course, it is not appropriate to analyze dead cells, but this could potentially be solved by using a shorter treatment duration than 24 hours wherein fewer cells die."

This is a good point. To address it, we have now replaced this panel with a time point where most cells are still alive (20 h, 0.2 µM Era2), as suggested by the reviewer (Fig. 3E,F). This did not change the conclusion that BODIPY-C11 oxidation decreases with cell size.

Reviewer #3: "2) In Figure 5, are the small, medium, and large bins for ACSL4 KO cells the same as for WT cells? If the ACSL4 KO cells are just bigger to begin with, this could explain why the "small" bin has greater cell survival than the WT small bin. Moreover, is the overlap between the three bins the same in the WT and KO cells?"

This is an important point that we now address with data shown in Fig. S4B. We have now added a Supplementary Figure S4B to show the relative size of small, medium, and large WT and ACSL4 KO HMEC cells. As seen from this graph, the ACSL4 KO cells are not bigger than WT cells. Importantly, the fold-range between the small and large FACS-sorted cells is similar (~1.9 to 2-fold).

Reviewer #3: "3) Loo, et al. Nat Comms 2025 similarly found that senescent cells (which are enlarged) are resistant to ferroptosis using the same inhibitor as the authors. In contrast to the authors, they show that this is due to lysosomal alkalinization and sequestration of ferrous iron in lysosomes. Given that Lanz et al. 2022 found that lysosomal components super-scale with cell size, it seems like this would be an important hypothesis to address. Free lysosomal iron can be easily measured with the LysoRhoNox stain. Loo et al. was able to restore ferroptosis sensitivity in senescent cells using the V-ATPase activator EN6, so it would be important for the authors to address whether this (or similar) treatment would have the same effect in enlarged cells."

This is an excellent point. We have now performed this experiment and added it to the manuscript, as suggested by the reviewer. Based on the Lyso-FerroRed staining (another brand name for the LysoRhoNox probe), we do not see an increase in lysosomal iron sequestration in large cells (Fig. S2B) - see the graph and the corresponding discussion below:

Line 301: "Previous work suggests a link between increased sequestration of ferrous iron in lysosomes and resistance to ferroptosis. It was reported that senescent cells, which are also large (Fig. S3A,B), gain resistance to ferroptosis through lysosomal alkalinization and sequestration of ferrous iron in lysosomes (Loo et al, 2025). We therefore tested whether the superscaling of lysosomes observed in large cells (Lanz et al, 2022; You et al, 2025) promotes Era2 resistance through lysosomal iron sequestration. To do this, we stained the cells with the lysosomal iron detection probe Lyso-FerroRed (Saimoto et al, 2025) and measured its scaling using flow cytometry (Fig. S2B). We observed that the amount of Lyso-FerroRed, and therefore, the amount of lysosomal iron, scaled in direct proportion to cell size, just like the total cellular protein content (Fig. S2B). These results indicate that iron chelation by ferritin and its sequestration in lysosomes are unlikely to play a crucial role in size-dependent decrease in Era2 sensitivity."

Reviewer #3: "Minor concerns:

1) It would be helpful if this manuscript were re-submitted with line numbers to more easily reference the text."

We have added line numbers for convenience.

Reviewer #3: "2) In Figure 5A and other figures that reproduce data from Lanz et al. 2022, it would be helpful to have a summary curve for the overall abundance of each protein rather than only the individual peptide curves. These plots (particularly Figure 5A) are difficult to interpret since some peptides were presumably more abundant / measured with higher confidence than others."

We have added the average ACSL4 protein slope line to Fig. 5A.

Reviewer #3: "3) In Figure 5, the authors show the validation of the ACSL4 KO HT-1080 cell line but not HMEC, even though both are used in this figure. It would be useful to show both. Additionally, the authors switch back and forth between the two cell lines for this figure, and it is not clear why."

We have added the HMEC ACSL4 KO validation Western blot in Fig. S4A (see below).

For the BODIPY oxidation experiment (Fig. 5D), we used HT-1080 instead of HMEC because HT1080 cells are sensitive to lower concentrations of Era2, and therefore, we could better optimize the Era2 concentrations and treatment durations to measure BODIPY oxidation at the time point when most cells are still alive but demonstrate a pronounced oxidized BODIPY signal.

Reviewer #3: "4) In Figure 5B, the authors use antibody-based staining of ACSL4 and flow cytometry to correlate a loss of ACSL4 expression with increased cell size, validating the proteomics data in Figure 5A. This does not seem like a good way to do this. Firstly, fixing cells with formaldehyde alters their size (is this proportional across differently sized cells? It's impossible to know), which makes it inappropriate to use SSC as a proxy for size in this particular situation. Secondly, the normalization scheme here doesn't make sense. If actin was used as a reference protein, why was tubulin used to normalize ACSL4 abundance? Overall, this seems like a very round-about experiment that could have just been addressed by doing a simple western blot with the four size bins sorted from live cells (as it was in the proteomics). If the issue is that ACSL4 is not detectable by western in the HMEC cells, another solution would be plating the live, sorted bins on coverslips and measuring by IF (or using the HT-1080 cells)."

We prefer IF flow cytometry to Western blotting for protein scaling analysis because it is more quantitative and provides cell size and protein content information for each individual cell. While in principle, different-sized cells might change their size differently during fixation, the cells that were larger or smaller prior to the fixation remain larger or smaller after fixation as well. Therefore, the SSC measurement after fixation still provides reliable information on size ranking, even if SSC does not perfectly linearly scale with cell volume. We do not use the SSC information to calculate protein concentrations here. Instead, we divide the amount of our protein of interest in the cell by the amount of constitutively-expressed Tubulin, which acts as an analogue of a loading control in this experiment. In Fig. 5B, both ACSL4 and Actin were normalized to Tubulin to estimate their concentrations. Actin is used just as a reference protein to show how the concentration of a perfectly scaling protein remains constant across cell size, as opposed to the sub-scaling ACSL4. Tubulin in this case was used as a proxy for total cellular protein content, which scales linearly in proportion to cell volume. This approach for determining the scaling behaviors of different proteins was previously validated in Lanz et al., Mol Cell 2022.

Reviewer #3: "5) In Figure 5E/5F, the authors pre-arrest the cells in G1 with palbociclib before size-sorting them. The pre-arrest is not done in other experiments using this cell line for size-sorting, so it would be important for the authors to comment on why this was done for this experiment but not others."

As we found in Fig. 2B-E, the cell cycle has confounding effects on size-dependent ferroptosis susceptibility measurements (as discussed in detail in our response to the first major point of Reviewer #1 above). Briefly, to avoid these confounding effects and isolate the effects of cell size from the effects of the cell cycle, we pre-synchronized the cells with 24 h treatment with palbociclib in Fig. 5E,F. This is now better clarified in the text, as follows:

Line 456: "In this experiment, we synchronized cells in G1 phase using palbociclib prior to cell sorting and also incubated the sorted cells in the presence of palbociclib during Era2 treatment to isolate cell size effects from the previously observed confounding effects of the cell cycle on ferroptosis (Fig. 2B,E)."

Reviewer #3: "6) Conceptually, it is difficult for me to understand why large cell size sensitizes cells to GPX4 inhibition but confers resistance to Era2 treatment. Particularly given the pathway described in Figure 3A, I am having trouble understanding why these would convey such opposing phenotypes. Shouldn't the extra ferritin in the bigger cells also help them cope with GPX4 inhibition if, as the authors state in the discussion, the increased sensitivity to the GPX4 inhibitor is reported to be mediated by (among other things) iron accumulation? A deeper discussion of this seeming-incongruity would be helpful for contextualizing the broader role of cell size in determining ferroptosis sensitivity."

We agree this is an important point, which was also raised by the other reviewers. As such, we note that context-dependent (i.e., cell type-specific) effects are common in the ferroptosis field, and multiple groups including our own (Dixon) have published extensively on genes and mechanisms that can lead to differences between erastin2 and RSL3. For example, there are studies showing that the mTOR pathway or the p53 pathway can both prevent and promote ferroptosis, depending on the cell type or some other hidden variable.

To better address the differences between Era2 and RSL3 in the context of the cell-size-dependent response, we have now added more data and discussion. In the Results section we added panel 4B and the following text:

Line 359: "While the upregulation of GSH biosynthesis may promote the resistance of larger cells to ferroptosis, such an upregulation alone cannot explain why larger cells become more resistant to ferroptosis induced by the cystine import inhibitor Era2, but not, for example, by the GPX4 inhibitor RSL3 (Chan et al, 2025) (Figs. 2B, S1B). We found previously that upon mTORC1 inhibition cells can evade cystine deprivation-induced ferroptosis by uptake and catabolism of cysteine-rich extracellular proteins, mostly albumin (Armenta et al, 2022) (Fig. S3C). This process involves albumin degradation in lysosomes, predominantly by cathepsin B (CatB), and subsequent export of cystine from lysosomes to fuel the synthesis of glutathione. Large cells undergo proteome rearrangements similar to those occurring upon mTORC1 inhibition (Zatulovskiy et al, 2022). This suggests that large cells may upregulate CatB expression to bypass the Era2-induced cystine import inhibition via system xc-. To test this hypothesis, we used flow cytometry to measure how the expression of cathepsin B and the system xc- cystine/glutamate transporter SLC7A11 (xCT) scales with cell size (Fig. 4B). We found that SLC7A11 concentration modestly decreases, while CatB concentration significantly increases with cell size (Fig. 4B). This shift in the ratio between SLC7A11 and CatB supports the hypothesis that larger cells may rely less on cystine import via system xc- and thus become more resistant to system xc- inhibition by Era2."

Figure 4. (B) Flow-cytometry-based measurement of cystine/glutamate transporter SLC7A11 (xCT) and cathepsin B (CatB) concentrations in G1-phase RPE-1 cells demonstrates a modest decrease in SLC7A11 and a significant increase in Cathepsin B concentrations with cell size. To calculate the concentrations of SLC7A11 and CatB, their amounts were measured with flow cytometry using immunofluorescence and normalized to the amounts of α-Tubulin. The data were binned by cell size, and mean values for each bin were plotted against normalized cell size (solid blue line for SLC7A11 and red line for CatB). Shaded areas denote the s.e.m. for each bin.

Additionally, in the Discussion we added the following:

Line 578: "We show that large cells may become resistant specifically to Era2 but not RSL3 through the upregulation of lysosomal function, particularly cathepsin B expression, which enables the uptake and catabolism of cysteine-rich extracellular proteins. A size-dependent shift in the ratio between SLC7A11 and cathepsin B makes large cells less dependent on cystine import via system xc-, and thus, more resistant to Era2. In addition to this, it was reported that RSL3 can induce ferroptosis independently of GPX4 and may target other selenoproteins (DeAngelo et al, 2025; Cheff et al, 2023), which could also contribute to the difference in size-dependent responses to RSL3 and Era2."

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, Zatulovskiy and colleagues elaborate on their previous work describing cell size-dependent changes in the proteome by investigating whether these changes can be correlated in differences in cell physiology. Using a cleverly-designed high throughput screen, they searched for compounds that differently-sized cells display differential sensitivity towards. Their primary hit, Era2, is involved in the ferroptosis pathway and serves as the starting point for a detailed study of how excess cell size protects cells from ferroptosis-induced cell death via: 1) lower concentrations of ACSL4 (which produces peroxidation-prone PUFAs), 2) increased ferritin concentrations, and 3) increased GSH concentrations.

Overall, the experiments in this manuscript are well-designed and interpreted. It is an extremely well-written manuscript with a clear trajectory of logic. I have only a few major concerns that should be addressed before publication:

Major concerns:

1) In Figure 3E, the authors gate their flow cytometry data using SYTOX so that they are only analyzing live cells. Based on their gating scheme, it seems like there are really a lot of dead cells. Presumably the cells that died were the most sensitive to Era2, so it seems an oversight to discard these cells. Of course, it is not appropriate to analyze dead cells, but this could potentially be solved by using a shorter treatment duration than 24 hours wherein fewer cells die.

2) In Figure 5, are the small, medium, and large bins for ACSL4 KO cells the same as for WT cells? If the ACSL4 KO cells are just bigger to begin with, this could explain why the "small" bin has greater cell survival than the WT small bin. Moreover, is the overlap between the three bins the same in the WT and KO cells?

3) Loo, et al. Nat Comms 2025 similarly found that senescent cells (which are enlarged) are resistant to ferroptosis using the same inhibitor as the authors. In contrast to the authors, they show that this is due to lysosomal alkalinization and sequestration of ferrous iron in lysosomes. Given that Lanz et al. 2022 found that lysosomal components super-scale with cell size, it seems like this would be an important hypothesis to address. Free lysosomal iron can be easily measured with the LysoRhoNox stain. Loo et al. was able to restore ferroptosis sensitivity in senescent cells using the V-ATPase activator EN6, so it would be important for the authors to address whether this (or similar) treatment would have the same effect in enlarged cells.

Minor concerns:

1) It would be helpful if this manuscript were re-submitted with line numbers to more easily reference the text.

2) In Figure 5A and other figures that reproduce data from Lanz et al. 2022, it would be helpful to have a summary curve for the overall abundance of each protein rather than only the individual peptide curves. These plots (particularly Figure 5A) are difficult to interpret since some peptides were presumably more abundant / measured with higher confidence than others.

3) In Figure 5, the authors show the validation of the ACSL4 KO HT-1080 cell line but not HMEC, even though both are used in this figure. It would be useful to show both. Additionally, the authors switch back and forth between the two cell lines for this figure, and it is not clear why.

4) In Figure 5B, the authors use antibody-based staining of ACSL4 and flow cytometry to correlate a loss of ACSL4 expression with increased cell size, validating the proteomics data in Figure 5A. This does not seem like a good way to do this. Firstly, fixing cells with formaldehyde alters their size (is this proportional across differently sized cells? It's impossible to know), which makes it inappropriate to use SSC as a proxy for size in this particular situation. Secondly, the normalization scheme here doesn't make sense. If actin was used as a reference protein, why was tubulin used to normalize ACSL4 abundance? Overall, this seems like a very round-about experiment that could have just been addressed by doing a simple western blot with the four size bins sorted from live cells (as it was in the proteomics). If the issue is that ACSL4 is not detectable by western in the HMEC cells, another solution would be plating the live, sorted bins on coverslips and measuring by IF (or using the HT-1080 cells).

5) In Figure 5E/5F, the authors pre-arrest the cells in G1 with palbociclib before size-sorting them. The pre-arrest is not done in other experiments using this cell line for size-sorting, so it would be important for the authors to comment on why this was done for this experiment but not others.

6) Conceptually, it is difficult for me to understand why large cell size sensitizes cells to GPX4 inhibition but confers resistance to Era2 treatment. Particularly given the pathway described in Figure 3A, I am having trouble understanding why these would convey such opposing phenotypes. Shouldn't the extra ferritin in the bigger cells also help them cope with GPX4 inhibition if, as the authors state in the discussion, the increased sensitivity to the GPX4 inhibitor is reported to be mediated by (among other things) iron accumulation? A deeper discussion of this seeming-incongruity would be helpful for contextualizing the broader role of cell size in determining ferroptosis sensitivity.

Significance

Strengths: well-designed study, clear results that are broadly in line with other recent studies on the same topic.

Limitations: opposing results between Era2 and GPX4i (which should in theory cause similar phenotypes) call into question how broadly cell size impacts ferroptosis susceptibility / indicate that this may occur in a limited context

Advances: first study to show that enlarged cells might have higher antioxidant capacity

Audiences: cell size researchers, ferroptosis/cell death researchers

My expertise: cell cycle checkpoints, cell size control, proteomics

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Referee #1

Evidence, reproducibility and clarity

Summary:

The study by Zatulovskiy et al. examined how cell size influences cell susceptibility to ferroptosis. The authors found a size dependence specifically for ferroptosis-inducing drug Era2, but not for other drugs. Using various human cell lines (HMEC, HT 1080, RPE 1), the authors generated populations of small and large G1 cells by FACS, CDK4/6 inhibition (palbociclib), or inducible cyclin D1 knockdown, and measured cell susceptibility to ferroptosis. Larger cells were more resistant than smaller cells. Mechanistically, larger cells showed reduced plasma membrane lipid peroxidation, higher glutathione concentrations, and changes in relevant cellular proteins levels, as analyzed using previously published data. Deleting ACSL4, which is involved in ferroptosis, partly eliminated the size dependence of ferroptosis. The work concludes that cell size is a key determinant of ferroptosis susceptibility.

My major concerns about this work focus on whether many of the results reflect cell size or cell cycle effects, and whether the FACS-based size-scaling analyses have some misleading features to their design & presentation. If these concerns can be addressed with new experiments, then the conclusions of this paper are justified. If these concerns cannot be addressed, then the authors should more directly acknowledge the alternative hypothesis that cell cycle effects may explain many of their results.

The experiments seem to be replicated sufficiently, and most conclusions rely on data from multiple cell lines. My minor comments focus on needs to provide statistics and method details, and on suggestions on how to improve text clarity, but these edits are easily done and don't require new experiments. Overall, this is an interesting study, and it should be published once the concerns below are addressed.

Major comments:

• In experiments reported in Fig 1 and 2A, the authors sort small and large cells in G1, plate them, and later start the drug treatments & cell monitoring. Are these cells actively cycling (progressing in the cell cycle), and how fast? The large cells are likely to enter S phase earlier than the small cells, so by the time that the authors start their drug treatments, they may be comparing cells in different cell cycle stages, which could influence drug sensitivity more than cell size (as the authors also suggest later in Fig 2). This needs to be controlled for. Furthermore, even if the cells remain in G1 after sorting until the drug treatments are started, the authors should address the fact that the drugs are present for a long time, thus targeting the cells in various cell cycle stages.
• Can the G1 arrest-driven changes in drug susceptibility (Fig 2 C-D) be attributed to cell size? Can the authors rescue the palbociclib treatment with rapamycin or other growth inhibitors that allow size to remain small during G1 arrest?
• In Fig 2E-F, is the cell cycle distribution of the samples influenced by CCND1 shRNA induction? Are the drug sensitivity effects due to cell size or cell cycle changes?
• Can the authors address the meaningfulness of the FACS-based size-scaling results in cases where cell-to-cell variability is very large? For example, in Fig 4D&G, the results are so variable even in identically sized cells that the importance of the size-scaling pattern seems questionable.
• In Figs 4B-D, the cell size axis seems to have over 4-fold size variability, but when the authors show the analysis of this data (Figs 4E-G) the variability is only 2-fold. What was excluded and on what basis?
• Based on the methods section & figure legends of Fig 4B-I, the RPE cells were not pre-sorted to include only G1 cells, nor did the assay account for cell cycle differences. How can these data be used to explain results from earlier figures, where analyses were exclusively focused on size differences in G1?

Minor comments:

• I recommend clarifying in the early introduction that all size changes discussed are in the absence of DNA content increase.
• The introduction seems to cite primary research and review paper in the same sentences, which is a bit misleading as the reviews don't seem to add new evidence.
• OPTIONAL In the second introduction paragraph, consider the classification/description of the three different mechanisms. Currently, it seems that these mechanisms are not independent of each other, and the details provided about each mechanism are inconsistent.
• Please provide statistics for the IC50 values reported based on Fig 1C. Were small and large cells statistically different? Are the IC50 values reported as +/- standard deviation or some other metric?
• OPTIONAL Providing more insight into why Era2 and RSL3 treatments yield more opposite responses would be of great interest to the field.
• Is the BODIPY-C11 labeling specific to plasma membrane, as suggested by the writing of the authors, or do the results shown integrate signals over all cell membranes?
• How exactly is gating done for the flow cytometry samples? Especially when analyzing size-scaling, the results are likely to be sensitive to outliers, such as those seen in Fig 4C (a subpopulation of very low CFSE stained cells). Can the authors clarify their methods and/or display supplementary figures with gating examples?
• In Fig 4, total protein staining was used as a control, whereas Fig 5B b-actin was used as a control. Why did the authors rely on different controls approaches for essentially the same measurements? Are these controls comparable?

Significance

I work in the cell size research field, and I am familiar with other related works in this field. My evaluation reflects a specialist's view of this study. Overall, this study will be of a large interest to a small group of specialists, and specific aspects of the work will also gain some interest from broader basic research audiences studying mechanisms of drug responses and ferroptosis in general. However, I do not see this work gaining very broad interest across larger audiences, simply because the field of cell size research is not of broad interest, and this is not a landmark study for the field.

The field of cell size research has long searched for size-dependent functions, as these could help explain why cell size matters. This study is a nice addition to our field, helping establish ferroptosis as a size-dependent function. However, the significance of this work relies on how clearly the authors can establish that their results are cell size rather than cell cycle effects (see major comments above). Should the authors address these concerns, then this study will provide some conceptual and mechanistic insight.

Regarding mechanistic insights, this work is in stark contrast to a recent study about size-dependency of ferroptosis (https://doi.org/10.1016/j.isci.2025.112363), where increased cell size heightened sensitivity to the GPX4 inhibitor RSL3, thus suggesting an opposite conclusion than what the authors observed with the drug Era2. The authors examined this contradiction, and while their results with the drug RSL3 agreed with the recent study, they did not explain why different drug mechanisms yield opposite results. Providing more insights into this discrepancy would increase the impact of this work.

Regardless of the impact of this work, I want to emphasize that I am fully supportive of seeing this work published once the technical concerns have been addressed. Our field will benefit from this work, and this work could catalyze important future research. The general topic studied here has the potential to become very important.

Reviewer #2 (Public review):

Summary:

This manuscript combines fMRI and EEG investigations performed at two research sites to examine 'willed' or volitional visuospatial attention, as contrasted with more standard cued (or 'instructed') visuospatial attention. The primary findings are: 1) willed attention (vs. instructed attention) drives additional cortical circuitry across a broad fronto-parietal network; 2) the direction of willed attention, but not instructed attention can be decoded from the pre-cue EEG data and from MVPA analysis of the trial-level fMRI data; and 3) the subjects with high EEG decoding also exhibited high neural efficiency (i.e., high decoding with low BOLD signal change) in the fMRI data. The methods and data analysis are generally sound, and these results appear solid. On the negative side, it is not made clear how the present findings extend our understanding beyond prior published work from one of the senior authors. There are also three significant concerns regarding interpretation of the findings. One has to do with the causal interpretation of the pre-cue alpha EEG signal determining the direction of willed attention. The second concern is the degree to which the present research paradigm adequately examines 'willed attention.' The third is that the MVPA analysis is not sufficiently described, and Permutation testing needs to be done to validate these findings. Otherwise, this manuscript appears methodologically sound, but questions about interpretation may mute the potential impact.

Strengths:

The focus on willed attention attempts to move beyond some of the many limitations of standard laboratory investigations of attention.

The shared paradigm across two modalities and two research sites demonstrates solid reproducibility, even though a few minor differences are observed across sites.

Weaknesses:

(1) There are concerns about this experimental paradigm carrying the banner of Willed Attention, because the application of 'Will' appears quite modest. Yes, extra brain activity is exhibited for this condition vs. its control, but do the cognitive processes isolated adequately stand in for 'Willed Attention?" Willed attention, as operationally defined here, appears to involve a simple decision process prior to the shifting of spatial attention. The cue is internally generated, but after that the rest of the attentional processes appear identical to standard externally cued visuospatial attention experiments. This self-generated cue process likely involves some sort of memory/history of the recently selected cues and then some random-ish selection between A and B. This appears very similar to asking the subject to guess whether a fair coin flip will be heads or tails on each trial. A mental 'coin flip' feels like a very weak version of 'will.' As a potential remedy, it would be helpful to discuss what other phenomena might fall within 'willed attention' and what some future studies might choose to focus on, along with some potential pitfalls (e.g., the reasons why the current study avoided more robust exemplars of will).

(2) The manuscript is lacking a description of the decision processes used during the willed attention paradigm and is lacking evidence as to WHEN subjects made their willed decision. Both of these points are of major concern:

(a) The authors state: "For willed attention, participants were explicitly told to avoid relying on any stereotypical strategies of generating decisions, such as always attending the same/opposite side they attended during the previous trial, as well as to avoid randomizing or equalizing their decisions to choose left or right across trials; prior studies found that decisions to explicitly randomize decisions might invoke additional working memory related processes (Spence & Frith, 1999)." Subjects were instructed NOT to apply a simple heuristic and NOT to randomize or try to equalize their decisions, but exactly HOW the subjects made their decisions is not at all clear. What options does that leave? How does this strategy avoid the working memory-related processes mentioned in the Spence & Frith, 1999 citation? The brain regions that comprise the network of interest (aka Frontoparietal Decision Network) are activated by a very broad range of visual cognitive tasks, including many working memory paradigms. The Anterior Insula and dACC nodes Salience Network often simply reflect task difficulty. Obviously, making a choice is more cognitively demanding than not making a choice. The present experiments do not distinguish functional roles between different regions of the Frontoparietal Decision Network. On the whole, the study does very little to isolate the cognitive processes or neural bases of willed attention beyond calling out the set of 'Usual Suspects' for visual cognition.

(b) The finding that pre-cue EEG signals predicted the postcue decision is intriguing. It could mean that the seemingly irrelevant and transient state of the brain causally and unconsciously biased the subject to one direction or the other. Alternatively, it could mean that the subjects utilized the pre-cue period to make their decision and hold it in case it was needed (i.e., that it was a choice trial). While 2-8 seconds ITI variability makes sense for fMRI decoding, it is a long time for a subject to idly wait, so they might fill that time preparing for the next trial. There appears to have been a substantial amount of individual difference in the pre-cue alpha decoding, which could reflect individual differences in cognitive strategy, specifically in the use of the pre-cue period to make their decision. More efficient decision makers might have pre-decided, which might account for the neural efficiency. The experiments lack any measurement of WHEN participants made their decision. For that reason, I would ask that the authors temper their claims about the significance of the alpha decoding and its possible causality.

(3) Did individual subjects exhibit a choice bias of location for the willed trials? If not, doesn't that raise concerns that subjects were trying to equalize their trials? If they do exhibit location biases, how does that impact the decoding? A simple decoder could learn to always just guess the biased direction for a subject and would perform > 50%. Consider the example in which an individual subject chooses 'Left' 55% of the time. A classifier that simply learns to choose 'Left' on every trial will be correct on 55% of trials. The training data would likely be sufficient to learn the direction of choice bias in each individual subject. So the classifiers could perform significantly above 50% without learning anything beyond the tendency of each subject. That is to say, 50% is not truly chance in this data set. It doesn't appear that Permutation testing has been performed to empirically determine chance for an individual's data. Permutation methods, scrambling the labels 1000 or 10000 times to establish a true baseline would be preferred over simply comparing to 50% and would address concerns about individual subject biases.

(4) The novel contributions of this work beyond the two prior Bengson et al papers from Dr. Mangun's lab appear quite modest. The discussion would be enhanced by specifically stating how the present work advances understanding beyond the prior Bengson studies.

Reviewer #3 (Public review):

Summary:

This manuscript analyzes two independent datasets collected at different sites. Using the same willed-attention paradigm (instructional vs. choice cues) and combining fMRI and EEG analyses, the authors investigate how attentional direction is selected when no external instruction is provided. Their main claims are that the dorsal attention network is engaged by both cue types, whereas the choice cue additionally involves a frontoparietal decision network. Moreover, left-versus-right attentional decisions can be decoded in this decision network only on choice trials, and multichannel pre-stimulus alpha patterns predict the subsequent attentional choice. Finally, individuals with more predictive alpha patterns show greater neural efficiency in the decision network, i.e., higher decoding with lower BOLD activation.

The question is worthwhile and the two-site design is a genuine strength. At the same time, several central inferences rely on decoding analyses for which the statistical testing and cross-validation structure are not described in enough detail to assess robustness. In addition, using a ratio-based neural-efficiency measure make the interpretation more fragile than it needs to be. With a focused revision that tightens inference around MVPA and clarifies a few methodological points, I think the paper could become substantially more convincing.

Strengths:

The work extends previous willed attention studies by attempting to link pre-stimulus alpha pattern predictability to post-cue frontoparietal representations, and by testing reproducibility across two datasets. The conceptual advance beyond previous studies, e.g., Bengson et al. (2015), however, depends on how solid the decoding-based evidence is and whether alternative explanations are convincingly excluded. At present, the strength of support is limited mainly by incomplete reporting and/or controls for MVPA significance testing, as well as potential inflation of decoding estimates if folds are not independent of run structure. Concerns about statistical assessment of decoding accuracy are well documented in the literature (Combrisson & Jerbi, 2015).

Weaknesses:

(1) The manuscript describes the decoding pipeline for both fMRI and EEG MVPA. However, it does not clearly specify how "significantly above chance" is determined for the fMRI ROI decoding, nor how multiple comparisons across ROIs are handled, even though p-values are reported. The same issue applies to the time-resolved EEG analysis across many time points. For each decoding analysis, please specify the inferential test (e.g., permutation test within participant, group-level test on subject accuracies, binomial test, etc.) and report effect sizes with confidence intervals (e.g., Combrisson & Jerbi, 2015). Further, for EEG decoding over time, it would be preferable to control family-wise error, e.g., cluster-based permutation, rather than thresholding pointwise p-values. A standard approach here is the nonparametric cluster framework (e.g., Maris & Oostenveld, 2007).

(2) The cross-validation approach used here is appreciated and appropriate in principle. However, random 10-fold splits across trials can inflate accuracy if training and test folds share run-specific noise, scanner drift, or autocorrelated structure. The manuscript should indicate whether folds were blocked by run or randomized across the entire session. In addition, please report the number of trials per condition after artifact rejection and after removing short ITIs for the long prestimulus epochs (−2500 ms to 0 ms) for each dataset in the section of EEG preprocessing. Similarly, please report how often participants chose left vs. right on choice trials, and whether balanced folds (or an equivalent balancing procedure) were used if needed.

(3) Moreover, ROI definition is not sufficiently specified and independence should be clarified. The ROIs are defined based on peaks from the choice-instructed univariate contrast (Table 2) and then used for MVPA. First, are these ROIs defined as spheres around peaks or using anatomical masks? What radius or voxel count was used? This needs to be explicit. Second, I am concerned about circularity risk. Although choice-vs-instructed selection is not identical to left-vs-right decoding, ROI selection from the same dataset can still bias descriptive estimates and encourages overinterpretation if not carefully justified (Kriegeskorte et al., 2009). At minimum, the authors should explain why their selection criterion is independent of the decoded contrast under the null, and ideally provide a robustness check using either anatomical ROIs or independently defined ROIs, e.g., from prior literature or an atlas.

(4) Using an index of neural efficiency is conceptually interesting. However, if the denominator, computed as the activation difference between choice and instructional conditions, is near zero or noisy, the ratio can become unstable. I would rather see a multivariate model that treats activation and decoding as separate dependent measures, or a latent-variable approach, than a single ratio.

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Reply to the reviewers

Reviewer 1

__#1.1 __In Fig 1 it appears that both PI3P and PI3,5P2 are present on lysosomes (Lamp1-FRB) and that recruitment of MTM1 (via FKBP) depletes both of them. Additionally, In the images and quantifications, it appears that after recruitment of MTM1, there is no vesicular pools of PI3P or PI3,5P2 left at all. This raises several concerns:

__#1.1a __What is happening to the pool of PI3P on Rab5 endosomes? The main pool of PI3P is on Rab5 endosomes and separate from LAMP1 lysosomes. Why does recruitment of MTM1 to lysosomes then lead to almost complete depletion of all PI3P (Fig1 B bottom panel), when the lysosomal pool of this lipid should be minor compared to that on early endosomes?

We plan to add data showing recruitment of FKBP-MTM1 to FRB-Rab5 positive endosomes. This also causes complete depletion of both PI3P and PI(3,5)P₂ probes. We believe this is the result of the over-expression of Rab5 or LAMP1 reporters, the robust activity of FKBP-MTM1 and the somewhat indistinct nature of these compartments (e.g. 10.1016/j.cell.2024.11.028) – in short, there is enough residual LAMP1 present in Rab5 enriched compartments or Rab5 in LAMP1-enriched membranes that robust depletion of lipids occurs in both when over-expressed .

__#1.1b __The main problem comes from disagreement with figure 3. There it is shown that ".PI(3,5)P2 does not significantly overlap with PI3P". If this is true, then why does recruitment of MTM1 to LAMP1 lead to the depletion of both PI3P and PI3,5P2. This would indicate that they are on the same compartment (LAMP1 positive lysosomes)?

We plan to add a complete, quantitative co-localization analysis of PI(3,5)P₂ and PI3P probes, as well as an analysis of both lipid probes with Rab5 and LAMP1. We already showed in such an analysis that PI3P is more closely co-localized with Rab5 than Rab7 (10.1083/jcb.201312072), but this is not absolute: not all late endosomal compartments are alike, and some contain PI3P whereas some do not (e.g. 10.1016/j.cell.2023.09.027). Likewise, we expect to show near exclusion of PI3P and PI(3,5)P₂, with greater co-localization between PI3P and Rab5 vs LAMP1, and the opposite for PI(3,5)P₂ (as shown in 10.1083/jcb.202408158). But nonetheless, there will be some PI3P-positive LAMP1 membranes.

#1.1c A merge and colocalization analysis is at least needed to address how much of SnxA and EEA1-FYVE is localized to LAMP1-FRB. But just by looking at the one cell depicted, the localisation of LAMP1-FRB seems to be rather distinct from EEA1-FYVE and SnxA

We believe our response to #1.1b will also address his point.

#1.2 Minor: Fig2 is all in all way to small and it is difficult to actually see the signal in panel A and C. It should also be noted that in these panels (zoomed in to my best ability) that there is clear localisation of SnxA to the plasma membrane. Is this pool lost after Apilimod treatment, or is this unspecific binding? This PM localisation also appears in Fig1 B and 5C and should be discussed.

We will enlarge the panels in figure 2 to ease visualization of the detail. We will also describe the PM localization of the probe, and how this is insensitive to apilimod treatment (Fig2. 2A). We will add this to the discussion, also citing how a non-PI(3,5)P₂ dependent PM localization of SnxA was also noted in the original study (Vines et al), and note this as a potential draw back of the full-length SnxA.

__#1.3 __It should also be pointed out that dextran will be taken up through macropinocytosis and might follow different endocytic trafficking to conventional receptor.

We will add a description to the results for figure 2 describing how dextran is taken up non-selectively through fluid-phase endocytosis (i.e. both conventional receptor-mediated endocytosis and micropinocytosis).

#1.4 It also seems that the dextran signal decreases after Ap treatment. Is this the case? Has this been quantified? Would that point towards the whole endocytic structure being degraded and not just PI3,5P2?

We believe this reduction is due to simple photobleaching of the dye under time-lapse imaging. We will quantify this as suggested – but crucially, we included the DMSO vehicle control which will perfectly control for photobleaching.

__#1.5 __OPTIONAL: The timeline of PI3,5P2 degradation and vacuolation is a great experiment and very important. However, PI3,5P2 production is critically dependent on prior generation of PI3P. It could be of interest to readers what happens to SnxA localisation when cells are treated with VPS34-IN-1 or Wortmannin. How does loss PI3,5P2 compare between the timing of PIKfyve inhibition and inhibition of PI3K that generate its substrate. The timescales of this might tell us something interesting about the timings of phosphoinositide conversions. Also, treatment with PI3K inhibitors is known to not lead to vacuolisation even though it does also lead to a loss of PI3,5P2, further indicating that there might be more to the vacuolation phenotype than just the loss of PI3,5P2. These experiments would add novelty and detail to the study but do not change the overall findings or conclusions.

This would indeed be an feasible experiment, but we do not believe the novelty would be significant: rapid depletion of PI3P with PI3K inhibitors has already been documented; notably, we demonstrated depletion of PI3P by wortmannin with a similar ~10 min time constant (10.1083/jcb.201312072) to the PI(3,5)P₂ depletion by apilimod reported herein. Since substrate depletion is ultimately an enzyme inhibitor, we would anticipate very similar kinetics for PI(3,5)P₂ depletion by apilimod vs wortmannin. However, if the reviewer and editor believe this experiment is essential, we could add it. We just do not believe it significantly strengthens the paper.

#1.6a: Major: Fig3: The distinct localisation of PI3P and PI3,5P2 looks convincing but does not seem to be in line with data in Fig1.

We believe our response to #1.1 addresses this point also.

__#1.6b __It should be clearly noted and discussed that the structure in Fig3 B is a nascent macropinosomes (the size and proximity to the PM make this clear) and this transition on macropinosomes as been well characterised in Vines et al 2023

We agree with the reviewer that this structure could easily be a macropinosome, though without a marker, we cannot definitively make this claim. Of course, the same logic applies to our erroneous declaration that this is an endosome (though HEK293A cells do possess some similarly very large, Rab5+ve sorting endosomes)! We will therefore amend the text to classify this as “an initially PI3P positive compartment”.

#1.7 Major minor: Figure 5 is a very powerful approach to produce a completely independent pool of PI3,5P2. As control, the PIKfyve-CCR-Kina construct should be recruited to mitochondria in the absence of the MavQ construct. This should lead to the generation of PI5P (the other known product of PIKfyve) without generating PI3,5P2. This would be a useful control to test that SnxA does not bind to PI5P. (As a side note, this method would be great to use to try and find a bone fide PI5P effector. Maybe by isolating mitos and sending them to Mass Spec after altering their PIP composition? But this is obviously a completely different story)

The is an excellent suggestion. We plan to add these experiments as a control for Fig. 5, though there will be nuanced interpretation – because we have no way of verifying PI5P generation by PIKfyve in the absence of a verified PI5PP biosensor. Furthermore, direct synthesis of PI5P by PIKfyve remains controversial (e.g. 10.1073/pnas.1203106109). Incidentally, we have attempted to co-recruit a PIP4K to convert any PI5P to PI(4,5)P₂, but this did not work.

#1.8 Major: Figure 6 is great work, but it must be discussed that SnxA is a constitutive dimer while the 2xPx is a monomer. Therefore, the SnxA dimer will also contain two fluorescent proteins and will therefore also appear brighter than the 2xPx. Therefore, the increased baseline of SnxA might just be due to its nature as dimer and not because it has a higher affinity to PI3,5P2 compared to the 2xPx. OPTIONAL: One way to clear this up would be to make a 2xPx construct that also contains 2 fluorescent proteins. Also, the increase in fluorescence should also be shown as normalized to the initial intensity. From the graphs in 6a it seems that both have an ~1.3 and ~1.5 fold increase?

We will add a discussion of the constitutive dimer nature of full-length SnxA. However, we disagree with the assertion that the dual GFP of the GFP-SnxA dimers accounts for the increased baseline labeling – since our quantification is based on the ratio of fluorescence at the membrane to elsewhere. Since there is a heavily diffuse signal of unbound probe, this diffuse pool is also dually labelled by the dimeric GFP-SnxA – in effect, the increased signal on membranes by dimeric GFPs is cancelled by the cytosolic dimers. We will clarify this point in the discussion.

#1.9 OPTIONAL (but important): It would be great to compare the recently described G13V mutant of SnxA that is reported to have a higher affinity to PI3,5P2 (Preprint, Nishimura et al 2025). These experiments would add novelty and detail to the study but do not change the overall findings or conclusions. But as the study sets out to find the best PI3,5P2 probe, this might be very important

This is indeed an important study. That said, the existence of this mutant does not change the overall importance of our demonstration here that PI(3,5)P₂ is both necessary and sufficient to recruit SnxA to membranes. We also feel that it is beyond the scope of our manuscript to perform detailed controls on the findings of another manuscript that itself has not passed peer review. However, we will add a point to the discussion about the likely impact of the G13V mutant.

#1.10 Minor: In the discussion it is stated that "Vines et al. showed SnxA to have higher affinity for PI(3,5)P2 in vitro compared to 2xPx-SnxA" The Kd (to model membranes with 5% PI3,5P2 in POPC background!) for SnxA there is 187+-13nM and for 2xPx 217+-7 nM. Taking the top and bottom ranges of the uncertainty intervals to 200nM and 210nM respectively. While this is still a slightly higher Kd for SnxA, I am unsure how physiologically relevant this difference is.

This is an excellent point, and we will amend the discussion to point out that the subtle differences in affinity likely don’t explain the enhanced performance of SnxA, as indeed the dual GFPs don’t as covered in #1.8.

__#1.11 __Minor: In the discussion it is stated that "But, we could observe a short temporal overlap between the two lipids within a single endosome, lasting only a few minutes". If this statement refers to Figure 3B, then it must be clearly stated that this a macropinosome and not be conflated with canonical endosomes

We will less precisely define these membranes as we did in response to #1.6b

__#2.1 __While the data are by enlarge backed up by the presented data, there are two instances in which controls do not show the desired properties in some figures (but do in others). Specifically, the kinase dead control construct experiments in Figures 4D and 5D suffer from a lack of localization of the FKBP-PIKfyve-CCR-Kinase-Dead construct to the Rab5 endosomes or mitochondria respectively. Without robust localization of the control kinase, the dependency on PI(3,5)P2 synthesis (as opposed to physical kinase mediated recruitment) cannot be excluded. The construct shows robust relocalization in Figure 6 when the 2xPx-SnxA is being evaluated. With the combined evidence shown in the paper, this does not create significant doubt about the overall conclusions, but this issue needs to be addressed.

We believe the poor apparent recruitment in figures 4D and 5D stems from two reasons; firstly, the signal to noise of the tagBFP-kinase construct is low (especially since the photodamaging 405 nm excitation laser must be used at low intensity of these time-lapse experiments). Therefore, one solution is to simply select example images to demonstrate recruitment where expression of TagBFP2 had better signal-to-noise. As can be seen from the quantification of data in figures 5 and 6, recruitment of FKBP-PIKfyve-CCR-Kinase and FKBP-PIKfyve-CCR-Kinase-Dead were very similar, but this was not so for figure 4; in this case, we will re-analyze the data to analyze only FKBP-PIKfyve-CCR-Kinase cells with similar recruitment to the dead for a direct comparison; if there is insufficient data, we will repeat the experiments to obtain balanced recruitment of both.

__#3.1 __In Figure 1B, the authors show a rapid depletion of PI3P upon recruitment of MTM1 to LAMP1-positive membranes. The apparent minimal overlap between EEA1-FYVE and LAMP1 signals in the images is intriguing. It would be helpful if the authors could comment on whether this reflects rapid membrane trafficking dynamics or nonspecific membrane targeting of MTM1. In addition, the lysosomal SnxA signal appears to decrease with somewhat slower kinetics compared to PI3P. A short clarification as to whether MTM1 is expected to directly dephosphorylate PI(3,5)P₂, or whether the observed reduction in PI(3,5)P₂ is secondary to depletion of its precursor PI3P, resulting in gradual turnover of the PI(3,5)P₂ pool. Clarification of this point would further refine the mechanistic interpretation, although this point does not detract from the overall conclusions.

The first part of this comment will be addressed by our response to #1.1. We will also add a discussion detailing how MTM1 itself has a somewhat controversial substrate selectivity, with the first report stating it was PI3P selective and did not hydrolyze PI(3,5)P₂ (10.1073/pnas.160255697), whereas a subsequent study found that it has robust activity against PI(3,5)P₂ (10.1016/s0960-9822(03)00132-5). Therefore, direct activity on PI(3,5)P₂ cannot be ruled out. Secondly, we will describe how our data and Pemberton et al showed that PIKfyve recruitment depletes PI3P, demonstrating that PIKfyve activity can outstrip VPS34 that makes PI3P. Therefore, in PI(3,5)P₂-positive, PI3P-negative membranes, it is possible that VPS34 is still active, but PI3P never accumulates because PIKfyve immediately converts it to PI(3,5)P₂.

#3.2. In Figure 3, the authors conclude that SnxA and FYVE do not overlap, but rather localize in close proximity. While this is an interesting observation, some degree of apparent overlap can be perceived in the images. Although the qualitative impression is largely convincing, inclusion of a quantitative colocalization analysis (e.g., Pearson's or Manders' coefficients) could further strengthen this conclusion.

We are planning to add precisely this analysis in response to #1.1b.

#3.3. In Figure 4D, SnxA localization is still detectable in cells expressing the kinase-dead PIKfyve construct. If endogenous wild-type PIKfyve is present, residual PI(3,5)P₂ production could explain this signal and influence the interpretation of the experiment. The authors should clearly state which cell lines were used and whether endogenous PIKfyve activity was present in each condition. This information should be provided consistently in the figure legends to avoid ambiguity.

We will clarify the results and legends to make clear that endogenous PIKfyve is indeed expressed in these cells, with either FKBP-PIKfyve-CCR-Kina or FKBP-PIKfyve-CCR-Kina-Dead. Will clarify that over-expressed catalytic PIKfyve fragments will not perturb endogenous PIKfyve activity, explaining basal SnxA localization in figures 4C and 4D.

好的，我们先一步步来分析这个题目。

原句是：<br /> He always has his shoes __ at the railway station.

1. 句子结构分析

这里考查 “have + 宾语 + 宾语补足语” 的用法。<br /> - 如果表示 “让某人做某事”，用 have sb do sth（美式）或 have sb to do sth（英式较少见，但此题不适用）。<br /> - 如果表示 “让某物被做”（让别人做，不是主语自己做），用 have sth done（过去分词表示被动）。<br /> - 如果表示 “让某物/某人一直保持某种状态或进行某个动作”，用 have sth/sb doing（现在分词表示主动且持续）。

2. 结合句意

“他总是在火车站让人擦鞋。”<br /> 鞋子是被擦的，所以逻辑上鞋子是 被擦亮，而不是鞋子自己“正在擦亮”别人。<br /> 因此要用 have sth done（让别人做某事）的结构。

“擦亮”鞋子，动词原形是 shine，过去分词是 shined（美式，特指擦亮鞋子）或 shone（一般指发光，不用于擦鞋）。<br /> 这里指“擦鞋”，所以过去分词用 shined。

3. 选项分析

(A) shone —— 过去分词，但意思是“发光”，不表示“被擦亮”，排除。<br /> (B) to shine —— 不定式，这里不是表示目的或将来，不符合“have sth to do”的惯用表达（have sth to do 表示“有某事要做”，主语自己做），这里主语是让别人做，所以排除。<br /> (C) shining —— 现在分词，表示主动或持续，但鞋子不会自己“正在擦亮”，逻辑不对，排除。<br /> (D) shined —— 过去分词，表示“被擦亮”，正确。

4. 简单解释与重点

简单解释：<br /> 这个句子意思是“他总是在火车站（让别人）擦鞋”。<br /> 英语里“have + 物品 + 过去分词”表示“让别人做这件事”。<br /> “擦鞋”的“擦亮”在美式英语里过去分词是 shined，所以选 (D)。

关键点：<br /> 1. have sth done = 让某事被做（别人做）。<br /> 2. 区分 shine 的过去分词：<br /> - shone → 发光<br /> - shined → 擦亮（鞋子等）<br /> 3. 根据句意，这里是被动含义，所以用过去分词 shined。

答案：(D) shined

好的，我们一步步来分析这道题。

原句：

We can go out now. It stopped __ quite a while ago.

1. 句子意思

“我们现在可以出去了。雨在好一会儿之前就停了。”<br /> 空格在 It stopped __ 后面，需要选择正确的动词形式。

2. 关键语法点

stop 这个动词后面可以接两种形式：

1. stop doing something
2. 表示“停止做某事”（停下正在做的事情）。

3. 例：It stopped raining.（雨停了 → 雨原来在下，现在不下了。）

4. stop to do something

5. 表示“停下来，去做另一件事”。
6. 例：He stopped to rest.（他停下来休息。）

3. 结合本题

句子说“雨在好一会儿之前就停了”，意思是“下雨”这个动作停止了。<br /> 所以要用 stop + doing 结构。<br /> rain 的动名词是 raining。

4. 选项分析

• (A) rain → stop 后面不能直接接动词原形，排除。
• (B) raining → 正确，stop raining 表示“停止下雨”。
• (C) to rain → stop to rain 意思是“停下来，以便下雨”，逻辑不通。
• (D) rained → stop 后面不能直接接过去式，排除。

5. 答案与要点总结

正确答案：(B) raining

关键点：<br /> - stop doing = 停止做某事（某事结束）<br /> - stop to do = 停下来去做另一件事<br /> - 这里“雨停”是“停止下雨”，所以用 stopped raining。

如果你愿意，我可以再给你出几道类似的练习题来巩固这个知识点。

好的，我们一步步来分析这道题。

原句：<br /> The witness went on the witness stand __ by the prosecution.

中文翻译：<br /> 证人走上证人席，______ 被检方。

1. 句子结构分析

• 主语：The witness（证人）
• 谓语：went on the witness stand（走上证人席）
• 空格部分：修饰“went on the witness stand”的目的或状态，并且后面有 by the prosecution（被检方）。
• “by the prosecution” 表示动作的发出者是检方，所以空格处的动词应该是被动关系。

2. 选项分析

(A) being questioned<br /> - 表示“正在被询问”，强调进行中的被动状态。<br /> - 但这里“went on the witness stand”是一个瞬间动作，用“being questioned”作状语时，通常表示伴随状态，逻辑上证人走上证人席时“正在被检方询问”不太符合常理（一般上了证人席后才开始被询问）。

(B) to question<br /> - 主动不定式：表示目的——“为了询问（别人）”。<br /> - 主语是证人，证人走上证人席是为了询问别人吗？不合理，因为证人主要是被询问的。

(C) to be questioned<br /> - 被动不定式：表示目的——“为了被询问”。<br /> - 符合逻辑：证人走上证人席，目的是被检方询问。

(D) questioning<br /> - 现在分词主动形式：表示主动询问别人。<br /> - 与 by the prosecution 连用会矛盾，因为如果是“questioning by the prosecution”应该是被动才对。

3. 关键点

• 看到 by the prosecution 就确定要用被动形式。
• 不定式可以表目的，这里最合理的目的是“为了被询问”。
• 因此正确选项是 (C) to be questioned。

4. 简单解释

这句话意思是：证人走上证人席，是为了被检方询问。<br /> “to be questioned” 表示“将要被询问”，符合证人席的功能。

答案：C ✅

好的，我们一步步来分析这道题。

题目原句：<br /> Americans ______ bacon and eggs for breakfast every day.<br /> 选项：<br /> (A) used to having<br /> (B) are used to have<br /> (C) are used to having<br /> (D) used to

1. 关键语法点

英语中有两个容易混淆的结构：

1. used to + 动词原形
2. 表示“过去常常做某事，但现在不做了”。

3. 例如：I used to play basketball.（我过去常打篮球。）

4. be used to + 名词/动名词

5. 表示“习惯于某事”。
6. 例如：I am used to getting up early.（我习惯早起。）

2. 分析句子意思

句子说“美国人每天早餐吃培根和鸡蛋”，这是描述一个现在的习惯或普遍现象，而不是“过去有但现在没有”的习惯。

所以不能用 used to + 动词原形（因为那是过去习惯，且暗示现在不这样了）。

应该用 be used to + 动名词 表示“习惯于做某事”。

3. 看选项

(A) used to having ❌（没有 be 动词，used to 后面不能直接接 having 表示习惯）<br /> (B) are used to have ❌（be used to 后面应接动名词或名词，不能接动词原形）<br /> (C) are used to having ✅（正确，表示“习惯于吃”）<br /> (D) used to ❌（后面缺动词原形，而且表示过去习惯，与句意不符）

4. 简单解释

• 句子想表达“美国人习惯于每天早餐吃培根鸡蛋”，所以选 are used to having。
• are used to = 习惯于（现在）
• having = 动名词，因为 to 在这里是介词，不是不定式符号。

答案： (C) are used to having

一句话总结：<br /> “be used to doing” 表示现在习惯做某事，符合句意“美国人习惯每天早餐吃培根鸡蛋”。

这个题目考查的是如何用英语正确、流畅地连接两个相关的动作或事实。

原句是：<br /> “__ the silkworm makes a liquid in its body and then squeezes it out through special holes.”<br /> 意思是：“__ 蚕在体内制造一种液体，然后通过特殊的小孔把它挤出来。”

简单解释：<br /> 横线后面是一个完整的句子（有主语 the silkworm，有动词 makes），所以横线上需要填一个能引出这个句子的成分，并且要和后面内容在逻辑上连贯。

选项分析：

1. (A) It makes silk<br /> 如果选这个，就变成 “It makes silk the silkworm makes a liquid...” 这会出现两个动词 makes 连在一起，语法错误，意思也不通。

2. (B) Making silk<br /> “Making silk, the silkworm makes a liquid...” 语法上可以，意思是“为了制造丝，蚕在体内制造一种液体……”，但英语里这种现在分词开头通常表示伴随或方式，这里逻辑是“目的是制丝”，用 Making silk 不太精确，但可接受。不过，更常见、更明确表示目的的是不定式。

3. (C) To make silk,<br /> “为了制造丝，蚕在体内制造一种液体……” 这是最清晰的表达“目的”的方式，语法正确，并且和后面句子连接自然。

4. (D) Silk is made by<br /> 如果选这个，就变成 “Silk is made by the silkworm makes a liquid...” 这样 by 后面接 the silkworm 本来可以，但后面又出现 makes，就重复谓语，语法错误。

关键点：<br /> - 从语法上，只有 (B) 和 (C) 能让句子完整。<br /> - 从逻辑和常见表达上，这里描述的是“蚕制丝的过程”，用 To make silk（为了制丝）来引出后面步骤是最自然、最符合英语习惯的。<br /> - 因此正确答案是 (C) To make silk,。

简单总结答案：<br /> 选 C，因为“To make silk”表示目的，能自然连接后面蚕的身体如何制造丝的过程，语法正确，意思清晰。

这是一道非常经典的不定式（to do）与被动语态结合的题目。正确答案是 (A) to be gentle and gracious。

我们可以用你之前学到的“还原法”和“助动词逻辑”来彻底拆解这道题：

1. 还原逻辑：从“据说”到“事实”

这句话的底层逻辑是一个关于“传闻”的结构。我们先把它还原成主动语态：

• 主动语态： His friends say **that** he **is** gentle and gracious.（他的朋友们说他很文雅。）
• 被动语态（形式主语）： It is said by his friends **that** he **is** gentle...
• 被动语态（主语提升）： He is said by his friends **to be** gentle...

2. 为什么用不定式 to be？

还记得你之前读到的吗？不定式 to 往往隐藏着一个助动词或一种“非确切事实”的语气。

当我们将 that 从句（事实陈述）转换为简单句时，原来的动词 is 不能直接跟在 said 后面（不能说 He is said is...）。

• 逻辑转换： 这里的 to be 承接了原来从句中 is 的含义。
• 语气含义： “据说”本身带有某种程度的推测或转述色彩（类似 it seems 或 it is believed），这种非直接观察到的状态，在英语中习惯用不定式 to 来连接。

3. 选项分析（排除干扰）

• (B) to have graciousness and gentle： 词性不匹配。and 连接的是并列成分，graciousness 是名词，gentle 是形容词，结构不对称。
• (C) gentle and a gracious man： 缺少动词。He is said... 后面如果没有 to be，句子就断了，无法连接后面的形容词。
• (D) that is a gentle and gracious man： 语法错误。如果用 that 引导从句，主语必须是形式主语 It（例如 It is said that...）。当主语是 He 时，后面不能直接接 that 从句。

4. 延伸：如果他“以前”很文雅呢？

根据你之前读到的“完成式表达过去”的逻辑，如果他的朋友们说他“以前（现在不一定了）”很文雅，这句话会变成：

He is said to **have been** gentle.

你看，逻辑是完全统一的：To + 原形表示现在的情况，To + have done表示过去的情况。

💡 总结

这类题目（is said to / is reported to / is believed to）考察的就是将从句转化为不定式的能力。

记住这个公式：

主语 + be said + to do / to be ...

需要我再给你出两道类似的“据说/看起来”结构的题目练习一下吗？

这是一道考察使役动词与固定短语结合的经典语法题。正确答案是 (D) made believe。

我们可以用你之前学到的“逻辑还原法”来拆解这个句子：

1. 核心短语：Make believe

在英语中，make believe 是一个固定短语，意思是“假装”（pretend）。

• 逻辑拆解： 这里的 make 依然遵循使役动词的逻辑。make believe 字面意思是“使（人）相信”。
• 为什么不带 to？ 就像你之前读到的，使役动词 make 具有强制性，要求结果是确定的（我要让你信，你就得信），因此排除了代表不确定性的 to，直接接原形 believe。

2. 时态的一致性：过去时

观察句子的前半部分：

Not wishing to attend the dance...（因为不想参加舞会……）

这是一个分词结构，描述的是过去发生的背景。主句的主语是 Marie。

• 既然 Marie “假装”生病是过去发生的事，动词 make 必须变成过去式 made。
• 后面的 believe 依然保持原形，因为它受使役动词 made 的支配（使役动词 + 宾语 + 原形，这里省略了宾语或将其合一）。

3. 为什么其他选项不对？

• (A) made believed： 错误。make（使役动词）后面必须接动词原形，不能用过去分词 believed。
• (B) make believe： 时态错误。这是原形，不能表达过去发生的动作。
• (C) makes believe： 时态错误。这是第三人称单数现在时。

4. 深度理解：句子还原

按照你喜欢的“还原法”，这句话可以理解为：

Marie made (people) believe that she had a fever. （玛丽使人们相信她发烧了 $\rightarrow$ 玛丽假装发烧了。）

总结

这道题其实是两个知识点的交汇：

1. 使役动词强制性： make 后面接原形（不带 to）。
2. 动作发生时间： 整个事件发生在过去，所以 make 变 made。

下次看到这类题目，你可以先找“谁让谁做”，如果没有 to 且时态正确，那就是它了！需要我再找几个类似的使役动词练习题考考你吗？

好的，我们先一步步来分析这个题目。

原题：<br /> Not wishing to attend the dance, Marie __ that she had a fever.<br /> 选项：<br /> (A) made believed<br /> (B) make believe<br /> (C) makes believe<br /> (D) made believe